Energy supply and dense energy storage

When can a lithium-ion cell design search trust a reduced battery model (SPMe) instead of the full DFN model?

research/cell-fidelity

Research programme on fidelity-aware Li-ion electrode design; paper discussion (7j): drift-score triage of PyBaMM DFN cell designs saves 19% of DFN cycles out of batch, which is 17% of wall time if flagged runs are continued from cycle 10 but a 4% loss if they are restarted, because the rule flags 76% of designs and a DFN run's fixed cost is worth about 5.7 cycles

414 tests

What it found

Paper discussion section (7j): the triage saving priced in wall time from timings already logged with committed runs. On 192 designs run both to cycle 10 and to cycle 100, a DFN run's fixed cost is worth 5.66 cycles (IQR 4.65 to 6.18; 2.63 on a second runner). The frozen threshold rule flags 76% of designs, so its 19.1% saving in DFN cycles is 17.1% of wall time when a flagged run is continued from cycle 10, and a 4.3% loss when it is restarted from cycle 0 (break-even at 72% flagged): the rule pays only in a toolchain that can resume runs, which this programme has not yet tested.

Three figures drawn from the tables. Descriptive, computed after the fact. Paper results section (7i): milestones 5zk to 7h written up with tables regenerated from the committed summaries by one command. Pooled over the two fresh pools (7g, 7h), 7f's frozen threshold policies meet the tail target in 18 of 24 (0.75; Wilson 95% 0.55 to 0.88; set-clustered bootstrap 0.67 to 0.88) at 40.5 DFN cycles per design, 19% saved against all-50 (bootstrap 12% to 27%). On 20 leave-one-pool-out folds the threshold and uniform rules each meet 19; the threshold rule is cheaper on 14, dearer on 4 (exact sign test p = 0.031), but its mean saving of 4.5 cycles per design has a bootstrap interval over the four parameter sets of −8.5 to +0.25. Intervals computed after the fact.

Milestone 7h (a fifth fresh pool): on 64 DFN designs simulated for this step only, 7f's 12 frozen threshold policies meet the tail target (1.25 × the all-50 upper quartile of cycle-99 lithium-loss error) in 9 of 12 for the second fresh batch running, at 39.3 DFN cycles per design against 50 (21% saved). Leaving each of five pools out in turn, the drift-score threshold meets 19 of 20 at 43.5 cycles (13% saved), a uniform run length 19 of 20 at 48.0 (4%). A threshold relative to the batch's median drift score meets 4 of 4 sets at 40.6 cycles but does not steady the flagged share (refuted), so the absolute threshold stays.

Show the rest of the summary (96 more paragraphs, 8,126 words)

Limits: 16 designs per fresh pool, 4 parameter sets, modelled fade only.

Milestone 7g (a fourth fresh pool): on 32 DFN designs simulated for this step only, 7f's 12 frozen nested-margin policies meet the fresh pool's tail target (1.25 × the all-50 upper quartile of cycle-99 lithium-loss error) in 9 of 12 with a drift-score threshold and 9 of 12 with a flag fraction, at 41.7 and 40.5 DFN cycles per design against 50 (17% and 19% saved, against 7f's 20%); refit on three pools the threshold rule meets 3 of 4 sets at 41.2 cycles, the uniform rule 4 of 4 at 47.5.

Limits: 8 designs per fresh pool (effectively 4 tests); the drift score's scale rose on two sets' fresh designs.

Milestone 7f (an out-of-batch margin): 7e's triage policy, chosen on two design pools, met the third pool's target in 4 of 12 folds. With the margin chosen by nested leave-one-pool-out, an absolute threshold on the drift score meets 9 of 12 and a flag fraction 10 of 12, both at 40.0 DFN cycles per design against 50 for all-50 (20% saved); the uniform rule's margin always lands on 50 cycles (12 of 12, 0% saved), and widening the flagged fraction alone meets 6.

Limits: 8 to 12 designs per pool, the drift score's fit saw every pool, no fresh fourth pool yet.

Milestone 7e (the triage frontier): over tail-error targets of 1.00 to 2.00 times the all-50-cycle upper quartile, flagging designs by 7c's ten-cycle drift score and extending only those saves 55%, 61%, 33% and 46% of the all-50 DFN cycles on Ai2020, Chen2020, OKane2022 and NCA_Kim2011 (uniform run lengths 36%, 39%, 27%, 18%; random flags 48%, 52%, 30%, 31%), chosen in hindsight within each set. A 30-cycle extension cannot reach 1.25 times the 50-cycle tail on three sets.

Picked on two design pools and applied to the third, the policy met the target in 4 of 12 folds (uniform 7 of 12), so the savings are an in-sample ceiling. H273 and H275 supported, H274 and H276 refuted.

Milestone 7d (flag and extend): the real ten-cycle forecast of cycle-99 lithium loss misses by 11.4% at the upper quartile on Chen2020 (5.7% with a 50-cycle line). Extending to cycle 50 only the designs 7c's ten-cycle drift score flags meets 1.25 times the all-50 tail error with 15% of designs extended (68% of the DFN cycles saved; random flags 40%), and on NCA_Kim2011 with 45% (44% against 20%); on OKane2022 no score, not even a hindsight oracle, saves much (85% to 95% extended). With every input measured, cycle-2 plating depth alone flags best on LG M50 (64% saved). Pre-registered: H269, H271, H272 supported, H270 inconclusive.

Milestone 7c (the per-design drift): with every input measured, each LG M50 design's fade-law drift over cycles 10 to 99 tracks the plating-weighted depth at cycle 2 (Spearman ρ = 0.80 on Chen2020 and OKane2022, Holm p = 0.0003; plating nearer the separator speeds the rate up). A leave-one-out correction on it leaves the set-median cycle-99 lithium-loss error near 2% (typical drift 4%, about the correction's own error) but, post hoc, halves the upper quartile (8.0% to 3.5%, 7.3% to 3.0%); on the real ten-cycle forecast it beats the line on all four sets. H265, H268 supported, H266 refuted, H267 inconclusive.

Milestone 7b (the law floor): with every input measured, the set-median cycle-99 lithium-loss error on LG M50 moves only from 1.8% to 1.6% (Chen2020) and 1.9% to 1.4% (OKane2022) as the law's line window grows from 10 to 50 cycles, while the real ten-cycle forecast falls from 5.6% to 2.7% and 6.7% to 2.1%: longer windows fix the inputs, not the law. The measured R(L) is linear in cycle number at the set median but drifts ±5 to 10% by design, so a borrowed curvature hurts; on Ai2020, whose R accelerates on every design, it cuts the floor from 8.3% to 4.8%. H261 supported, H263 inconclusive, H260, H262, H264 refuted.

Milestone 7a (held-out error budget, the paper's table): 5zu's Shapley split of the ten-cycle lithium-plating forecast error, repeated on 64 PyBaMM DFN designs no earlier step used, keeps every direction: the anode OCP rise is the largest input on OKane2022 and NCA_Kim2011, the drift on Chen2020, the capacity factor adds nothing, and on Ai2020 measuring the inputs makes the forecast worse (2.9% to 8.3%). But with all inputs measured the forecast still misses cycle-99 lithium loss by 3.4% on OKane2022 and 3.2% on Chen2020 (1.5% and 1.4% in sample), so out of sample over half the LG M50 error is the law's ten-cycle line. H256 to H259 supported.

Milestone 5zz (second fresh pool): on 32 more PyBaMM DFN designs, the per-node anode thickness line, fitted on all 72 earlier designs and used only inside their thickness range, beats the uniform node lever's set-median cycle-99 lithium-loss error on NCA_Kim2011 only (5.3% to 3.7%) and is worse on Ai2020 (1.2% to 3.4%), Chen2020 and OKane2022 (5.1% to 6.2%); it wins 14 of 29 in-range designs and 33 of 64 over both fresh pools. The design's own measured anode OCP rise beats the uniform lever on only 14 of 32, so outside NCA_Kim2011 the lever is not the forecast's limit. H254 supported; H252, H253, H255 refuted.

Milestone 5zy (held-out node gains): node-gain profiles learned on 5zk's 40 designs, applied to 32 fresh PyBaMM DFN designs (8 per set, run to 100 cycles), still read the cycle-99 anode OCP rise better than the uniform lever on every set; the per-node thickness line has the lowest set-median ten-cycle lithium-loss error on three of four sets (OKane2022 7.2% to 5.6%, Chen2020 7.5% to 6.5%, NCA_Kim2011 3.3% to 2.5%; Ai2020 4.4% to 5.0%) but beats the uniform lever on only 19 of 32 designs, missing two thin OKane2022 designs by 14 to 15%. The pre-registered monotonicity gate fired on NCA_Kim2011 only. H248 and H251 supported, H249 and H250 inconclusive.

Milestone 5zx (design-matched node gains): taking the borrowed late node-gain profile from the three nearest designs in design space (leave one design out, 40 PyBaMM DFN designs) keeps OKane2022's cycle-99 lithium-loss forecast at 4.5% error (uniform lever 6.7%) but leaves Chen2020 (6.5% against 5.4%) and NCA_Kim2011 (4.1% against 3.0%) worse, no better than 5zw's set median; the neighbours sit 0.6 to 0.75 of the design cube apart. A per-node line in anode thickness, reported after the plan, reaches 2.7% on OKane2022 and 1.5% on NCA_Kim2011, at or below the measured-OCP ceiling, and fails on Ai2020 and Chen2020, where the separator node's late gain is not monotone in thickness. Pre-registered H246 supported, H244 and H245 refuted, H247 inconclusive.

Milestone 5zw (node-gain transfer): carrying the median per-node gain profile of the other designs in a set (leave one design out, 40 PyBaMM DFN designs) takes the ten-cycle forecast of cycle-99 lithium loss on OKane2022 from 6.7% to 4.1% error (the measured-OCP ceiling is 3.5%) and reads the anode OCP rise better than the uniform lever on all four sets, but Chen2020 (5.4% to 6.5%) and NCA_Kim2011 (3.0% to 4.2%) get worse and only 23 of 40 designs improve.

Milestone 5zv (per-node gains): a gain per anode node on the node lever's uniform stoichiometry shift, fitted over cycles 3 to 10 of 40 PyBaMM DFN designs, takes the cycle-99 lithium-loss forecast on Chen2020 from 5.4% to 3.9% (the measured-OCP ceiling) and on NCA_Kim2011 from 3.0% to 2.3%, but on OKane2022 its gains (0.1 to 0.8) over-correct and the forecast stays at 6.9% against 6.7%; 22 of 40 designs improve, and gains on the separator-side nodes only (found after the plan) are a lead at 4.1%, on 6 of 12 designs.

Milestone 5zu (the error budget): scoring all eight forecast-or-measured combinations of the node lever's OCP rise, the non-OCP plating-overpotential drift and the charge-capacity factor on 40 PyBaMM DFN designs, a Shapley split gives the OCP rise 3.3 of the 5.6 points between the ten-cycle forecast and the all-measured diagnosis on OKane2022 (drift 1.1), the two 2.1 and 2.0 on Chen2020, and the factor under 0.3 on every set; on Ai2020 measuring the inputs makes the forecast worse (2.3% to 8.0%).

Milestone 5zt (the drift tie): tying the non-OCP drift of the plating-weighted plating overpotential to the falling charge overpotential forecasts its cycle-99 value in 40 PyBaMM DFN designs within 3.5 to 6.0 mV (a ten-cycle line: 7.1 to 13.0), but added to the node lever it worsens the cycle-99 lithium-loss forecast on all four sets (7.6% against 5.4% on Chen2020) and beats the law's lever on 17 of 40 designs; the measured drift takes Chen2020 to 2.4% but leaves OKane2022 at 6.5%.

Milestone 5zs (the capacity factor is done): a saturating ten-cycle fit of the charge overpotential in the electrode-balance window forecasts the cycle-99 charge-capacity factor of 40 PyBaMM DFN designs within 2.4 to 4.8% on all four sets (a ten-cycle line: 3.6 to 7.6%), and the node lever fed the measured factor itself changes its cycle-99 lithium-loss error by at most 0.7 points on three sets; with the saturating factor the node lever beats the law's own lever on 22 of 40 designs. The remaining ten-cycle error on LG M50 (5.4 to 7.6%) is the plating-overpotential lever.

Milestone 5zr (the capacity factor is the electrode balance): the open-circuit electrode-balance window with a ten-cycle line in the charge overpotential forecasts the cycle-99 charge-capacity factor of 40 PyBaMM DFN designs within 3.6 to 7.6% on all four sets, where a straight line missed by 16 to 51%, and the law's own factor is within 2.4 to 7.1%; the effective charge overpotential falls by 6 to 18 mV over ten cycles rather than growing. Fed to the forecast law with the node lever it beats the law's own lever on 14 of 40 designs and is no better than the node lever alone, so the remaining ten-cycle error on LG M50 is the lever.

Milestone 5zq (ten-cycle forecasts of the two inputs): extrapolating the non-OCP plating overpotential drift and the charge-capacity factor from cycles 2..10 of 40 PyBaMM DFN designs, the forecast misses cycle-99 lithium loss by 5.7% (Chen2020), 7.2% (OKane2022), 10.1% (NCA_Kim2011) and 7.0% (Ai2020), against 8.2, 5.9, 2.2 and 8.3% with the law's own lever and 1.1 to 8.0% with both inputs measured; it beats the law's lever on 15 of 40 designs. The capacity factor accelerates after cycle 10 on every set and the drift turns over, so straight lines cannot carry them.

Milestone 5zp (what bends the law's line): fed the measured plating-weighted plating overpotential rise and the measured charge-capacity factor of 40 PyBaMM DFN designs, the ten-cycle forecast at αF/RT misses cycle-99 lithium loss by 1.4% (Chen2020) and 1.5% (OKane2022), against 3.8 and 3.4% with the measured OCP rise alone, and the line's bend falls from 0.10 and 0.09 to 0.03 and 0.04; either input alone does little, and on Ai2020 the overpotential doubles the bend (4.2 to 8.7%). A 10× finer table changes nothing. Diagnoses that read cycle 99, not forecasts.

Milestone 5zo (lever or law): fed the measured plating-weighted anode OCP rise of 40 PyBaMM DFN designs, the forecast law at αF/RT with a ten-cycle line misses cycle-99 lithium loss by 3.8% (Chen2020), 3.4% (OKane2022), 1.2% (NCA_Kim2011) and 4.2% (Ai2020), against 8.2, 5.9, 2.2 and 8.3% with the law's own lever; the remainder is the law's line, whose R slope drifts 9 to 13% between early and late cycles. The node lever's OKane2022 over-read sits at the separator-side nodes, where the plating is (collector half's share 0.21). H209 supported, H210 inconclusive, H211 refuted.

Milestone 5zn (where the plating lever should be read): on 40 PyBaMM DFN designs the plating sits 0.04 to 0.22 stoichiometry above the forecast law's window top; reading the law's lithium-to-stoichiometry shift at each node's cycle-2 stoichiometry reproduces the plating-weighted OCP rise with slope 1.00, 0.98, 0.84 and 1.18 by cycle 99 (the law's own lever needs 1.35 to 1.49 on LG M50), and on Chen2020 from cycle 10 (3.25 against 2.88 mV measured, 0.42 for the law). At αF/RT the ten-cycle forecast with it beats the law's on Ai2020 (8.3% to 2.3% error) and Chen2020 (8.2% to 5.9%) and loses on OKane2022 and NCA_Kim2011 (22 of 40 designs); H204 to H208 inconclusive.

Milestone 5zm (how early the plating exponent can be read): cut at 10, 20 or 30 PyBaMM DFN cycles, 5zl's plating-weighted lever gives an exponent 2 to 3 times what LG M50 needs (100 and 49 to 75 against 38 and 34 at cycle 99), because the OCP where the plating sits rises several times faster than the law's lever while the law's window is on the graphite plateau; it is flat from cycle 10 on NCA_Kim2011 and settles by 30 on Ai2020.

Early-exponent forecasts lose to αF/RT given the same cycles on 4 of 4 sets at 10 cycles and 3 of 4 at 30; fitting the law's line over 30 to 50 cycles at αF/RT halves the error or better on every set. Pre-registered: H200, H202 refuted, H201, H203 inconclusive.

Milestone 5zl (what sets the plating exponent): on 40 PyBaMM DFN designs run to 100 cycles, αF/RT times the ratio of the plating-weighted end-of-charge OCP rise to the forecast law's own lever lands within 3 to 12% of the exponent the forecast needs on LG M50 and NCA_Kim2011, and 34% high on Ai2020; it beats the separator-node reading on 37 of 40 designs and cuts the 100-cycle forecast error threefold on LG M50 (a diagnosis: it reads cycle 99). It reverses 5zk's cross-pool reading. Pre-registered: H198, H199 supported, H195 to H197 inconclusive.

Milestone 5zk (where the plating is): on 40 PyBaMM DFN designs run to 100 cycles, the separator-side node carries only 8 to 19% of a cycle's plating (plating-weighted depth 0.53 to 0.72 of the thickness), which explains why a separator-node rate index mis-tracked NCA_Kim2011's slowdown (0.28 in log). Read where the plating is, the potential lever shrinks to 0.64 of the separator node's on Ai2020 and 0.78 to 0.81 on LG M50: the implied exponent moves from 73 to 47 on Ai2020 (needed 21) and away from what Chen2020 and OKane2022 need. Pre-registered: H191, H192, H194 supported, H193 refuted.

Milestone 5zj (where the lever goes): on PyBaMM's Ai2020 set, the intercalation overpotential and the charge-profile shape give back about 41% of the separator-surface OCP lever (about 20% on LG M50, −19% on NCA_Kim2011). That halves the exponent the lever implies there (73 to 43, against the 21 the forecast needs) but moves the other three sets further from theirs, so the plating exponent is not set at the separator node (post hoc, on 5z's committed records).

A ten-cycle lithium ledger re-confirms 5p and 5za: Ai2020's loss is plating, which PyBaMM 26.10.1.1 books for one of its 34 parallel electrode pairs. The integrated side-reaction current matches the particles' loss to 0.01%, and a doubled mesh moves it by 0.1%.

Milestone 5zh (calibration budget): resampling the 768 committed designs, a plating exponent calibrated on ten earlier 100-cycle runs matches the 160-run calibration in the median on all 24 pools (within 0.007), and ten runs from one earlier campaign do as well as scattered ones; but at the 90th percentile ten runs still lose to αF/RT on 10 of 24 pools (3 at 80 runs), and one run loses on all 24. H178 to H180 supported, H177 and H181 refuted; seen data only.

Milestone 5zg (per-set plating exponent): calibrating the plating law's kinetic exponent once per parameter set, as the median oracle κ* over the set's earlier 100-cycle DFN runs, cuts the cycle-99 lithium-loss error on 128 fresh designs from 9.3% and 7.6% to 4.9% and 6.5% on LG M50 and improves both controls (5.6% to 4.9%, 1.7% to 0.9%); pre-registered H172 to H176 supported.

Limits: 160 calibration runs per set, one current per set, modelled fade.

Milestone 5zf (kinetic exponent): on 128 fresh designs (four sets, 100 DFN cycles, SEI + plating, seed 24) a per-design plating exponent κ estimated from cycles 2 to 10 forecasts the cycle-99 lithium loss worse than the physical αF/RT = 25.3 V−1 on all four pools (LG M50 0.127 and 0.122 against 0.099 and 0.059 median |ln err|); LG M50's potential lever rises under 1 mV in ten cycles, so κ is not identifiable there.

The oracle κ that makes the forecast exact is 45 and 32 V−1 on LG M50 against 20 and 23 on Ai2020 and NCA_Kim2011: the law's lever is too shallow on LG M50. Modelled fade, one PyBaMM version.

Milestone 5ze (overpotential diagnosis): on 128 fresh designs (four sets, 100 DFN cycles, SEI + plating, seed 23) 5zd's η-window law replicates on LG M50 (0.109 and 0.095 median |ln err| against 0.191 and 0.160 for 5zc) and keeps its Ai2020 cost (0.063 against 0.024). Feeding the law η's true drift to cycle 99 is worse on all four pools (Ai2020 0.111); a discharge/charge split of η from the ten-cycle discharge energy puts the charge side within 2 to 5 mV of the symmetric η and moves the error by at most 0.007. On 384 seen designs, extrapolating η's ten-cycle trend and choosing the reading per design also fail. So the remaining gap is in the law's structure. Modelled fade, one PyBaMM version.

Milestone 5zd (consistent levers): reading the negative potential rise at the top of the η-shortened charge window, the same η 5zc measured from the charge Ah of cycles 2 to 10, cuts the cycle-99 lithium-loss error on fresh LG M50 pools (Chen2020, OKane2022, 64 designs, 100 DFN cycles, SEI + plating) from 0.202 and 0.167 to 0.104 and 0.064 median |ln err|, 59 of 64 designs won, with no new parameter; the separator-surface potential rise is forecast within 21 and 17 mV against 35 and 27 mV. NCA_Kim2011 improves (0.033 to 0.020), Ai2020 worsens (0.025 to 0.076) because its η drifts; rank correlation on LG M50 dips (0.97, 0.94). Modelled fade, one PyBaMM version.

Milestone 5zc (loaded charge): replacing the open-circuit capacity in 5zb's kinetic law with the capacity between the cut-offs less an effective overpotential η, measured from each design's charge Ah in cycles 2 to 10, cuts the cycle-99 lithium-loss error on fresh LG M50 pools (Chen2020, OKane2022, 64 designs, 100 DFN cycles, SEI + plating) from 0.279 and 0.248 to 0.210 and 0.161 median |ln err|, winning on 64 of 64 designs, with Ai2020 0.030 and NCA_Kim2011 0.023 unchanged; a constant η predicts the cycle-99 charge Ah within 4 to 7%, against 20 to 86% for the open-circuit capacity. Post hoc, charge Ah plus the measured separator-surface potential rise make the LG M50 plating rate steady, so the surface rise is what is left to forecast. Modelled fade, one PyBaMM version.

Milestone 5zb (kinetic law): with the plating per cycle proportional to the open-circuit charge capacity and slowed by the negative potential rise, the integrated loss is linear in the cycle count. A line fitted to cycles 2 to 10 forecasts the cycle-99 lithium loss on four fresh pools (128 designs, 100 DFN cycles, SEI + plating, new currents) better than the earlier power law on every pool and on 122 of 128 designs: Ai2020 0.076 against 0.150 median |ln err|, NCA_Kim2011 0.024 against 0.078, LG M50 0.24 to 0.26 against 0.31 to 0.33, ranks 0.98 to 0.999. The LG M50 residual matches the loaded charge shrinking faster than the open-circuit capacity says. Modelled fade, one PyBaMM version.

Milestone 5za (surface feedback): on two fresh LG M50 pools (Chen2020, OKane2022, 64 designs, 100 DFN cycles with SEI + plating) the ten-cycle forecast with the plating feedback read at the separator-side particle surface over-predicts the cycle-99 lithium loss by 21 to 23% against 35% for the open-circuit reading, no constant fitted, ranking kept (Spearman 0.96); it misses the 15% bar and does harm on NCA_Kim2011 and Ai2020, where it predicts the surface rise exactly yet errs more, so the open-circuit predictor works there partly by compensation. Ai2020's unbooked lithium is PyBaMM's side-reaction totals omitting its 34 parallel electrodes (5p); corrected, plating is 99.6%.

Limits: one current, offset from cycles 2 to 10, modelled fade.

Milestone 5z (mechanism): on 24 re-run LG M50 designs (Chen2020, OKane2022, 100 DFN cycles with SEI + plating) the per-cycle plating falls about 3.3× from cycle 2 to 99 because the negative electrode's open-circuit potential at the separator-side particle surface rises 38 mV at end of charge, where the open-circuit window used by milestone 5x moves only 0.5 to 9 mV; the same term carries the slowdown on NCA_Kim2011. Plating is 99.8% of the lost lithium there, and a one-node rate index tracks the plating change within 0.015 log units. (5z's note that only 3% of Ai2020's loss is booked is the parallel-electrode count; 5za.)

Limits: seen designs, one node, modelled fade.

Milestone 5y (fresh pools): on 192 new designs run 100 DFN cycles, the plating feedback exp(−αFΔU/RT), with no fitted constant and one power law fitted to the feedback-free loss on every pool, brings the cycle-99 lithium loss to within 2.4% and 3.8% on two NCA_Kim2011 pools and 10.2% on Ai2020 (uncorrected law 31%, 30%, 18%) and removes 5x's double count on Ai2020. Its energy ranking beats an 8-run calibration on NCA_Kim2011 (Spearman 0.82, 0.93 against 0.62, 0.84) but trails 5x's uniformly biased forecast on Ai2020 (0.875 against 0.974), and raw cycle-10 energy ranks at 0.93 to 0.96 on all three pools.

Limits: two cell sets, the law form chosen on seen pools, SEI treated as plating, OKane2022's plating parameters, modelled fade.

Milestone 5x (deriving the correction): PyBaMM's irreversible plating rate falls as exp(−αFΔU/RT) when lost lithium raises the negative electrode's potential at top of charge (α = 0.65). Applied to the first ten DFN cycles with no fitted constant, it brings the cycle-99 lithium loss on two NCA_Kim2011 pools to within 5.6% and 3.1% of DFN (ten-cycle law 27%, 30%) and ranks 100-cycle energy at 0.69 and 0.91, above 5w's 8-run calibration (0.51, 0.76). Over ten committed pools (622 designs) it orders the fitted slopes correctly (Spearman 0.92) and beats the √cycle energy fit on 10 of 10, but under-predicts Ai2020's loss by about 27% (the √n law already bends) and gives no feedback on the LG M50 sets, whose graphite sits on its plateau. Pools seen in aggregate; SEI treated as plating.

Milestone 5w (the correction on other cells): on fresh NCA_Kim2011, Chen2020 and OKane2022 pools (192 designs, 100 DFN cycles each, 56 held out per pool) the balance map fed the ten-cycle lithium law with 5v's self-limiting correction, its intercept recalibrated on 8 designs and its slope kept from Ai2020, ranks the 100-cycle energy at Spearman 0.76, 0.94 and 0.94, against −0.42, 0.80 and 0.80 for 5n's √cycle energy fit (beats it in 149 of 150 calibration draws).

The slope is cell-specific (0.34 to 0.37 on the two LG M50 sets, 0.58 on Ai2020), so the cycle-99 lithium loss is off by a median 8.5% there, and on these pools raw cycle-10 energy already ranks at 0.93 to 0.96, so they do not test the screen. Modelled fade (PyBaMM 26.10.1.1, OKane2022's plating parameters on every set), not measured cells.

Milestone 5v (a self-limiting correction, fresh pools): on 5u's committed pools the ten-cycle lithium law already ranks the cycle-99 DFN loss at Spearman 0.98 to 0.99, but the balance map is ill-conditioned (a 10% random error on the true loss drops its energy ranking from 0.96 to 0.38 to 0.67) and the law's size error grows with the fraction of lithium lost. One line, ln(Llaw/LDFN) = 0.658 + 0.577 ln(Llaw/nLi), fitted on 5u's three Ai2020 pools and frozen, was pre-registered on three fresh Ai2020 pools (64 Sobol designs each, seed 15; 192 DFN runs to cycle 100, 189 scored).

The corrected map ranks the 100-cycle energy at 0.92, 0.96 and 0.96 (5n's √cycle energy fit 0.67, 0.62, 0.59; uncorrected 0.61, 0.68, 0.82; fed DFN's own loss 0.96 to 0.97), gets the cycle-99 loss to a median 4% (uncorrected 11 to 18%), and with the raw top 4 finds the DFN best on every pool at 6.3 resumed designs against 7.7 for 5n's union. Refitted on 8 designs per pool the constants barely move (A 0.61 to 0.72, S 0.57 to 0.60).

Limits: one cell set, the one the constants came from; empirical, no mechanism fitted; three pools.

Milestone 5u (fresh pools, a per-pool loss law): the lithium-loss law picked per pool from the median ten-cycle power-law exponent (≥ 0.6: a + b√n, else a nb), then 5s's map, pre-registered on four pools no milestone had run (64 Sobol designs each, seed 14; 256 DFN runs to cycle 100, 241 scored). The selector picked as predicted, and the median predicted cycle-99 lithium loss was 1.05, 0.99 and 0.94 of DFN's on Ai2020 0.3×, 0.4× and 0.5× (1.32 on NCA_Kim2011@0.625×).

Fed DFN's own cycle-99 loss the map ranks the 100-cycle energy at Spearman 0.95 to 0.97 on all four pools. Fed the fitted law it ranks better than 5n's √cycle energy fit on only 1 of 4 (0.64 to 0.76 on Ai2020), predicts fade size better on 1 of 4, and as the union's fade list misses the DFN best by 1.25% on one pool where 5n's union is exact (5n's misses by 0.87% on another).

Per-design lithium ratios run from about 0.8 to 1.45 of the truth: the map is right, the pool law is right on the median, and the per-design ten-cycle fit is what loses the ranking. 5n's union stays the procedure.

Milestone 5t (a slowing lithium-loss law): 5s's map fed L(n) = a + b√n, fitted to the same ten DFN cycles and chosen on lithium alone from 27 designs run to cycle 100, scored pre-registered on the 13 committed pools those designs did not come from (no new simulation). It ranks the 100-cycle DFN energy better than 5s's power-law map on 12 of 13 (sign test p = 0.003) and better than 5n's √cycle energy fit on 8 of 13 (bar 9, mixed; by 0.23 to 0.33 on Ai2020@0.625×, Chen2020@2× and OKane2022@2×, worse on both NCA_Kim2011 pools); its fade size is worse on 7 of 13; and as the union screen's fade list it misses the DFN best by up to 3.2% where 5n's union is within 0.16%. 5n's union stays the procedure.

Milestone 5s (balance map as a fade predictor): 5r's electrode-balance map fed a power law L(n) = a nb through each design's lithium loss over ten DFN cycles, read at cycle 99. Pre-registered on 17 committed 100-cycle pools (1,108 fresh ten-cycle DFN runs, which reproduce the committed energies exactly): it ranks the 100-cycle DFN energy better than 5n's √cycle energy fit on 2 of 17 conditions, predicts fade size better on 7 (none of the eight Ai2020 pools), and as the union screen's fade list misses the DFN best by up to 6.9% where 5n's union is within 0.32% (all four hypotheses refuted).

Post hoc, on 27 designs run to cycle 100: fed DFN's own cycle-99 lithium loss the map is within a mean 0.02 to 0.05 of the fade on Ai2020, Chen2020 and NCA_Kim2011 (0.12 on OKane2022); the power law over-predicts that loss 1.2 to 2.8 times because plating's growth exponent falls from about 0.85 over cycles 2 to 10 to 0.24 to 0.63 by cycles 50 to 99. The balance map works; a cheap fade predictor needs a self-limiting lithium-loss law.

Milestone 5r (electrode balance): a map from the parameter set and the design alone (both electrodes’ lithium capacities, the cyclable lithium and the two OCP curves; the open-circuit window between the cut-offs and its energy) turns each DFN run’s own lithium loss into its energy fade with no fitted constant. Pre-registered on 128 fresh DFN runs (8 conditions, 8 new designs each, 20 cycles with and without degradation): within 0.05 of the degradation-added fade on 34 of 40 fading designs, mean error 0.038 against 0.053 for the best constant fade per lithium, a within-pool ranking at least as good as the lithium share on all 5 fading conditions (Ai2020@0.3× +0.95 against +0.48, @1× +0.81 against +0.21), and errors concentrated on designs far from open circuit (Spearman −0.73; NCA_Kim2011 over-predicted by up to 0.24). Fade splits into a design-only map and a lithium-loss rate; the map is fed DFN’s own loss, so it is a decomposition, not yet a predictor.

Milestone 5q (a two-cycle plating predictor): two SPMe cycles with SEI and plating on all 2,324 committed designs of 36 conditions, tested on the 24 conditions not read before the plan. The cycle-2 plating rate does not rank the 100-cycle DFN fade (median Spearman 0.03); a self-limited plating correction ranks designs worse than SPMe’s plain cycle-2 energy on 20 of 24; a top-half cut before the union screen missed by up to 6.1% and cost more than the screen it was meant to shorten; SPMe failed on 456 designs, the DFN best among them on 7 pools. Energy lost per unit of lithium lost varies about twofold within a pool, so a fade predictor needs an electrode-balance map.

Milestone 5p (what makes the designs fade): an ablation of PyBaMM's two degradation options on 8 committed conditions (128 DFN runs, 20 cycles). On the five that fade by 5 to 25%, the irreversible-plating submodel alone reproduces 0.998 to 1.015 of the fade and solvent-diffusion SEI alone 0.000 to 0.006; a closed form of PyBaMM's SEI law matches its lithium loss to under 10−4. PyBaMM 26.10.1.1's side-reaction lithium-loss variables under-count by the parallel-electrode count (34 on Ai2020, all 93 degraded runs). No earlier score changes; the programme's fade is OKane2022's plating kinetics, copied to six of seven sets.

Milestone 5o (a salt floor before any simulation): drop every design whose closed-form salt number rkt (0.04 s per design) is below −0.2, then run 5n's union screen on the rest. Pre-registered on three fresh pools (192 PyBaMM runs, NCA_Kim2011@0.875×, Chen2020@1.75×, Ai2020@0.875×): it dropped 25 to 35 of 64 designs, returned the pool's DFN best on all three, and took 0.48 to 0.79 of the union screen's time (0.15 to 0.20 of all-DFN).

The best design's rkt was never below −0.08 on 36 pools; a floor at 0 would have missed by 9.3%. The (energy, rkt) Pareto front is the wrong cut: on fade-limited Ai2020 the best sits on layers 4 to 7 and a 3-layer cut misses by up to 4.7%.

Milestone 5n (late fade from ten cycles): DFN to cycle 10 on every design, a least-squares line in √cycle through cycles 5 to 10 read at cycle 100, and the top 4 by that extrapolation together with the top 4 by raw cycle-10 energy resumed to cycle 100. Pre-registered on three fresh pools (192 PyBaMM runs, Ai2020@0.275× and @0.35×, NCA_Kim2011@1.25×): within 0.16% of the pool's DFN best on all three, where the raw 10-cycle screen missed by 9.2% and 3.9%; the extrapolation lifted the low-current Ai2020 ranking from Spearman 0.10 and 0.48 to 0.57 and 0.63, and is anti-correlated on NCA_Kim2011 (−0.68), where the raw list carries the pool; wall time 0.24 to 0.32 of all-DFN (bar 0.30, mixed); against 5m's ladder 0.16% worse on one pool, 0.39% better on another. Over 33 conditions the union is exact on 29, worst 0.32%.

Milestone 5m (successive halving over resumed runs): DFN to cycle 10 on every design, then the top 16 resumed to 20, the top 8 to 50 and the top 3 to 100. Resuming (PyBaMM starting_solution, 10-cycle chunks) reproduces uninterrupted runs bit for bit on 23 designs at 0.85 to 0.97 of their time. Pre-registered on three fresh pools (216 PyBaMM runs, Ai2020@0.3× and @0.4375×, Ecker2015@0.75×): exact on two, 2.7% short on Ai2020@0.3× where the 10-cycle screen missed by 8.8%, at 0.24 to 0.29 of all-DFN’s wall time (a run’s first ten cycles cost 15 to 17% of it). There the best design ranks 28th of 53 at cycle 10 and first only at cycle 50: designs that start best fade fastest.

Milestone 5l (retention from a short run): of the three factors of the 100-cycle score (thermodynamic energy, utilisation, retention), only retention needs simulation, and ten DFN cycles carry it. Pre-registered on three fresh pools (384 PyBaMM runs, Ai2020@0.625×, NCA_Kim2011@0.75×, OKane2022@1.75×): cycle-10 Wh/kg ranks cycle-100 Wh/kg at Spearman 0.92 to 0.97, and DFN@10 on all designs plus DFN@100 on the top 3 returned the DFN best on all three at 0.19 of all-DFN’s wall time; a sqrt-cycle fade extrapolation ranks worse. Known failure (development): Ai2020 at 0.25× and 0.375×, missed by 6 to 7%.

Milestone 5j (salt pre-screen in the search) runs DFN, not SPMe, on every design whose closed-form salt ratio rkt is at most 0.10, and keeps the trust rule and band stop for the rest. Pre-registered on two fresh pools (256 PyBaMM runs, OKane2022 at 1.25× and Chen2020 at 1.5× current): it returned the DFN-best design on both, at 1.12× and 0.90× the earlier procedure’s wall time (median 1.01× over 19 committed conditions), so it is not a saving.

It is a fix: on Chen2020@1.5× the earlier procedure stopped verifying inside the flagged block, one design short of the best (SPMe 19% low), and missed it by 4.5%. The best design’s rkt lay between −0.06 and +0.58 on all 21 conditions and below the flag on 8; discarding flagged designs would have missed by up to 17%, and a thermodynamic energy bound (never violated over 1,395 designs) prunes none of 429 flagged ones.

Limits: two fresh conditions on graphite cells seen at other currents, one machine’s timings.

Milestone 5i (closed-form trust flag) derives SPMe’s minimum salt ratio from the parameter set and the design alone: the steady electrolyte profile under SPMe’s uniform reaction, with concentration-dependent diffusivity handled exactly by the Kirchhoff transform. Pre-registered on the constant-diffusivity form over 1,280 committed designs (19 cell–current conditions): it ranks designs as SPMe does (Spearman 0.99) and predicts SPMe’s mis-scoring as well as the simulated flag (AUC 0.951 against 0.957), but over-predicts depletion (H66 mixed). The De(c) form, registered before 816 fresh PyBaMM runs were read, misclassifies 0 of 408 fresh designs (mean error 0.0003). It models SPMe’s electrolyte, not DFN’s (mean difference 0.03).

Milestone 6a (measured cells) checks SPM, SPMe and DFN against the measured constant-current discharges PyBaMM ships for the Kokam cell of Ecker et al. (2015, 1C and 5C) and the Enertech pouch of Ai et al. (2020, 0.1C to 2C). Pre-registered: SPMe is never closer to the measured capacity than DFN by more than 0.13 points (H61 supported); where SPMe’s r_min is at least 0.5 the two agree within 0.06% while both miss the cell by 0.9 to 4.3% (H63 supported); r_min does not order the SPMe–DFN gap across the two cells (Spearman −0.14, H62 mixed).

After the verdicts: the Ai cell’s logged temperature rise (1.6, 4.0, 10.4 K) matches PyBaMM’s lumped thermal model within 0.1 K; with heating the 2C SPMe–DFN gap falls from 1.50 to 0.32 points, and DFN’s 18.6 mV isothermal fit is heating error cancelling a 4% capacity offset. Default mesh, two cells, discharge only; no measured curve reaches the salt-starved designs where SPMe fails.

Milestone 5h (a gap-aware answer step) targets 5g's one miss: on Ai2020 at half current SPMe scored nearly every sound design about 24% low, so the answer step stopped 3.2% short of the DFN best. The band stop keeps verifying with DFN while some unverified design's SPMe score times q (the median DFN/SPMe ratio over verified designs with r_min > 0.1, floored at 1) could beat the verified best. Chosen on the 13 committed conditions, it was pre-registered and run on six new ones with fresh designs (788 PyBaMM runs: Ai2020 at 0.75× and 0.25×, NCA_Kim2011, Chen2020 and Ecker2015 at 0.5×, OKane2022 at 1.5×).

It returned the DFN best on all six at 0.33 to 1.07 of all-DFN wall time; 5g's iterate step did too, including Ai2020 at 0.75× where SPMe is 24% low (H58 refuted), so the band stop's extra 9 and 11 DFN runs on the Ai2020 pools bought nothing here. Over 19 conditions the iterate step misses on one (3.2%), the band stop on none. Rule recall stayed at or above 0.97; 13 Ai2020 DFN runs at 0.25× failed in the first cycle and were dropped. One PyBaMM version, 64 designs per condition, current the only condition varied.

Milestone 5g (skip SPMe or not, at new currents) pre-registers a gate that reads the first 8 SPMe runs of a pool and skips SPMe (running DFN on every design) when 4 or more fail or deplete their salt (r_min ≤ 0.1), and otherwise runs the 5e rule with an answer step that keeps verifying the merged leader. It runs on 64 fresh designs at six conditions no run had used (768 PyBaMM runs): OKane2022, Chen2020, Marquis2019, Ecker2015 and Mohtat2020 at twice the areal current density, Ai2020 at half.

Current moves the suspect share on every cell (Chen2020 0.25 to 0.81, Ecker2015 0.06 to 0.70, OKane2022 0.18 to 0.81, Ai2020 0.72 to 0.31 at half current). The gate chooses the cheaper branch on 4 of 6 (refuted): a structural SPMe failure costs under a second, so pools full of failures make SPMe cheap; the gated cost stays within 1.13× of the cheaper branch. The rule finds every mis-scored design at every condition. The answer is the DFN best on five conditions and 3.2% short on Ai2020 at half current, where SPMe scores designs a median 24% low and the best one is never verified (refuted). After the verdicts, a gate that also uses the SPMe-to-DFN time ratio from one DFN run is right on 12 of 13 conditions.

Milestone 5f (a pilot switch and a verified answer step) tests, on 64 fresh designs on each of Mohtat2020, Ai2020, NCA_Kim2011 and Ecker2015 (515 runs), whether 8 SPMe runs plus 2 DFN runs can tell when to skip SPMe and run DFN on everything, and whether verifying the leading design until it is DFN-scored returns the DFN best. The answer step does, in all 120 replayed trials; all 3 early SPMe stops re-solve at tight tolerance to within 0.2% of DFN; recall stays 1.00.

The switch fails its test: on Ai2020, where all-DFN is 11.6% cheaper, it fires in 20% of trials, because a salt cut-off of 0.10 misses mis-scored designs with minimum salt ratio up to 0.32. Across 11 cell pools the rule never costs more than 12% over all-DFN and saves 49 to 64% on six, so the recommendation is to run the rule every time. The switch constants were chosen on a post hoc replay of the seven committed cells.

Milestone 5e (the rule on new cells) fixes in advance the two-part rule from 5c and 5d (re-solve early SPMe stops at tight tolerance; DFN-verify failed runs, then the rest in ascending minimum salt ratio, until three sound) and runs it on 64 fresh designs on each of two cells it was not built on, Marquis2019 and Chen2020 (256 runs). On Chen2020 it verifies all 9 mis-scored designs in 15 DFN runs (23% of the pool), among them the DFN-best design, which SPMe scores 23% low and ranks 16th; Marquis2019 has no mis-scored design and costs 4 runs.

The planned answer step lands 1.3% below the DFN best on Marquis2019 because it compares verified DFN scores with SPMe scores that run 1 to 6% high at the top; taking the best verified design instead (chosen after the verdicts) reaches the DFN best on both cells. No run stopped early, so the re-solve step is untested.

Milestone 5d (why SPMe fails) re-solves, pre-registered, every SPMe run on the committed benches that failed outright (61: NCA_Kim2011 49, OKane2022 12) or stopped early (6, Mohtat2020) under four solver and mesh variants, with 24 completed runs as controls (455 runs). Tight tolerances (rtol 1e-6, atol 1e-8, IDAKLU or CasADi) finish all 6 early stops, which then score within 0.3% of DFN; more Newton iterations finish none. No setting gives any of the 61 outright failures a usable score: in 59 SPMe’s linearised salt concentration goes below zero in the first discharge (median −8% of initial), the charge step has no valid start, and PyBaMM discards the run. So stops are re-solved, failures go to DFN. All four hypotheses supported; V0 reproduces all 91 committed runs.

Milestone 5c (setting the cut-off on a new cell) compares, pre-registered, a trust-flag cut-off fitted to 8 random DFN runs with verifying designs in ascending order of SPMe’s minimum salt ratio until three sound ones in a row, on the three earlier cells and two new PyBaMM cells, Mohtat2020 and NCA_Kim2011 (64 Sobol designs each, 256 runs). On Mohtat2020 both fail (recall 0.00 and 0.17; H33, H34 and H37 refuted): its 6 mis-scored designs are SPMe runs whose solver stopped part-way (cycles 3 to 90), returned by PyBaMM as normal solutions, with no salt depletion.

Among SPMe runs that finish, r_min ranks the mis-scored designs at AUC 0.995 or better on every cell that has any. Flagging early stops as well (post hoc), bottom-up verification finds every mis-scored design on all five cells with 16%, 95%, 6%, 14% and 88% of the pool sent to DFN (mis-scored shares 13%, 89%, 2%, 9%, 81%), always fewer than the 8-run calibration (23% to 98%).

Milestone 5b (transfer) runs the trust flag and 9 frozen search methods, pre-registered, on two more PyBaMM parameter sets, Ecker2015 and Ai2020 (64 Sobol designs each, 384 runs, current scaled to the same areal density). SPMe's minimum salt ratio ranks the designs it mis-scores at AUC 0.995 on Ai2020 (57 of 64 mis-scored), but the OKane2022 cut-off r ≤ 0.07 misclassifies 20.3% there (best cut-off 0.33; H2 refuted); SPMe@10 no longer ranks DFN better than SPMe@100 (−0.01 and −0.11); the methods' ordering transfers (Spearman 0.73, 0.70), and the 2-cycle SPMe and DFN screens stay within 1.3× of the fastest method on all three cells while GP-EI is 1.9 to 3.7×. Cells are design-space variants (5% inactive rule, borrowed degradation parameters), not the published cells.

Milestone 5a (fresh designs) re-tests, unchanged and pre-registered, the post-hoc winners of parts 2b and 4b on 128 new Sobol designs (384 PyBaMM runs, same parameter set). On pools of 64 the whole-pool 10-cycle SPMe screen reaches a design within 1% of the DFN best in 122.9 s against GP-EI's 220.4 s and the SPM@2 screen's 205.0 s (both p < 0.001); SPMe@10 ranks 100-cycle DFN at Spearman 0.668 against 0.575 for SPMe@100; the 15 methods' medians correlate at 0.924 across the two design sets.

Cheap-start MF-UCB co-kriging beats GP-EI at every pool size but is 1.36× and 1.71× the best screen at 16 and 32 designs (refuted), and is fastest at 96. A 2- or 10-cycle SPMe screen stays within 1.4× of the fastest method at every pool size on both sets (descriptive). Same parameter set and protocol: transfer to other cells is untested.

Milestone 3 part 2b (where SPMe errs) models SPMe's residual against 100-cycle DFN as a function of SPMe's own minimum salt ratio r. The registered form -ln r, from the log in SPMe's electrolyte overpotential, halves the cross-validated error (21.3 to 11.3 Wh/kg) and beats (1 − r)2 and the 0.1 flag. As a planner, fitted on 16-design pilots, it lands within 2× of SPMe's DFN cost on only 2 of 4 cycle counts. As an online correction it is slower than milestone 1's flag rule (528 against 418 s).

Post hoc: SPMe@100's 14-call cost comes from the single DFN-best design, which is salt-depleted and drops from rank 1 at 10 cycles to 41 at 100. A plain whole-pool 10-cycle SPMe screen reaches a design within 1% of the DFN best in 123 s on pools of 64 and 172 s on 96, ahead of GP-EI (220 s) and every earlier screen. Exploratory: one parameter set, the same 128 designs. A research programme (proposal and log on the project page) on when a lithium-ion electrode design search can trust a reduced electrochemical model.

Milestone 4b (co-kriging multi-fidelity BO) replays autoregressive co-kriging over a cheap rung (SPM or 2-cycle DFN) and 100-cycle DFN, with augmented EI (Huang et al. 2006) and an MF-UCB fidelity rule (after Kandasamy et al. 2016), on the cached benchmark with measured run times. Started from five random DFN runs (122 s), no planned variant beats GP-EI (best 204.6 against 220.4 s on pools of 64; 267.1 against 220.4 s on 96) and all are far slower than whole-pool screening on small pools (157 against 46 s at 16 designs); three pre-registered hypotheses, two refuted.

Charging each design its own measured time keeps the method order (Spearman 0.90). Exploratory, chosen after the result: starting from ten 2-cycle DFN runs ties the best screen at every pool size (38, 90, 144, 174 s at 16, 32, 64, 96 designs) and beats GP-EI at each.

Milestone 3 (theory, part 2a) treats the screen’s residual as independent noise and gives an exact expected count of DFN runs (a one-dimensional integral for Gaussian noise). As a planner it calls whether whole-pool screening beats GP-EI right on 14 of 16 (screen, pool size) cases, against 8 of 16 for the worst-case formula; with one whole-space noise level it ranks the 11 screens only at Spearman 0.51 (refuted), 0.86 with the noise level near the top, because SPMe’s large errors fall on particular designs (on the DFN-best ones at 100 cycles: 14 DFN runs needed, 3 predicted).

Milestone 3 (theory, part 1) proves that screen-then-verify needs at most as many full DFN runs as there are designs within 2κ of the best, where κ is the screen’s worst residual after the best affine fit, so scale and shift errors are free; the bound held on all 330 (screen, pool) cases. Across 11 screens κ ranks the DFN calls needed at Spearman 0.72, the raw error at −0.07; SPM’s residual is a quarter of SPMe’s (11.0 against 42.8 Wh/kg) and SPMe’s tracks its own minimum salt concentration (Spearman −0.82). The worst-case cost formula built on it predicted screen against GP-EI on only 8 of 16 pool sizes (refuted).

Milestone 4 (search replay) replays 12 search methods on the cached benchmark, 30 pools of 64 designs, each simulation charged its measured wall time: screening every candidate with the plain SPM (100 cycles) or a 2-cycle DFN run and verifying in screen order reaches a design within 1% of the best 100-cycle DFN score in a median 153 or 160 s, against 220 s for GP-EI on DFN; the 10-cycle DFN screen takes 253 s (pre-registered H7, that it would need a third of GP-EI's time, refuted), successive halving over DFN cycles 247 s (185 s if runs resume), and milestone 1's trust flag cuts SPMe screening from 700 to 418 s. On pools of 96 GP-EI catches up, so whole-pool screening suits small candidate sets.

Milestone 2 (dense benchmark) runs 128 fresh space-filling (Sobol) designs for 100 cycles under SPM, SPMe and DFN (384 runs, every cycle kept): a 10-cycle DFN run ranks the designs by their 100-cycle DFN Wh/kg at Spearman 0.962 (95% 0.932–0.977), against 0.641 (0.480–0.789) for a full 100-cycle SPMe run, at the same wall time (3.6 s against 3.7 s), and its top 10 contain the DFN-best design, which SPMe ranks 41st. Unplanned: the plain SPM ranks better than SPMe (0.955; 0.984 against 0.769 over the 121 designs SPMe completes), though it over-scores the best design by 20 Wh/kg, and 15 of 128 designs (12%) are mis-scored by SPMe by over 25%.

Milestone 2a, the same question on the 49 stratified designs of energy-cell-dfn: 10-cycle DFN 0.977 against 0.834 for 100-cycle SPMe (paired bootstrap difference 0.138, 95% 0.057–0.271), and a linear fade extrapolation fails (Spearman 0.01).

Milestone 1: a 2-cycle SPMe run's minimum electrolyte concentration classifies the designs SPMe under-scores by more than 25% with ROC AUC 0.997 on the 49 (0.994 on the 128, whole-run minimum). Re-runs reproduce the committed SPMe and DFN scores exactly.

Limits: one parameter set and protocol, costs timed on one design and one 4-core machine, no measured cell for these designs.

Research log

Ongoing: each run adds a batch and an entry, newest first. Source: LOG.md.

2026-11-19 · Milestone 7j outcome: priced in wall time, the triage saving holds only if flagged runs are continued. A DFN run's fixed cost is worth 5.66 cycles (192 paired runs; 2.63 on a second runner), and the frozen threshold rule flags 76% of designs, so its 19.1% saving in DFN cycles is 17.1% of wall time when a flagged design's cycle-10 run is continued to cycle 50, and a 4.3% loss when it is restarted from cycle 0 (break-even at 72% flagged). Discussion section and three figures written

Show 140 earlier entries

2026-11-19 · Milestone 7j (paper step, plan): the discussion section, one figure per results table, and the triage saving priced in wall-clock DFN time. What does a modelling engineer get back, in CPU-hours rather than cycles, if they adopt the nested-margin threshold rule? (descriptive; no hypothesis is tested)

  • Planned: paper/figures.py (stdlib SVG, from paper/tables.json): Figure 1 for Table 1 (in-sample saving by rule and set), Figure 2 for Table 2 (hit rate with Wilson interval against DFN cycles per design for every out-of-batch look); paper/cost.py: seconds per DFN cycle from the seconds and ok_cycles fields of the committed bench.jsonl files (7g, 7h), per set, to convert 7g to 7h's cycle savings into time; paper/discussion.md (section 5).
  • Risks named now: bench timings come from a shared 3-worker cloud container, so they price relative time, not a workstation's absolute speed; runs to cycle 100 include the setup cost, which a per-cycle average spreads.

2026-11-19 · Milestone 7i (paper step): the results section, 5zk to 7h, with intervals. Pooled over the two fresh pools the frozen threshold policies meet 18 of 24 (Wilson 0.55 to 0.88, set-clustered bootstrap 0.67 to 0.88) at 40.5 DFN cycles per design (19% saved, bootstrap 12% to 27%); on lopo5 the threshold rule is cheaper than the uniform one on 14 of 20 folds (sign test p = 0.031), but a bootstrap over the four sets puts the mean saving of 4.5 cycles at −8.5 to +0.25

  • Written: paper/results.md (sections 4.1 to 4.8: pools and target, 7a's error budget, 7b's law floor, 7c's drift score, 7d and 7e in hindsight, 7e to 7h out of batch, results that did not hold, threats to validity); paper/tables.py regenerates Table 1 (in-sample) and Table 2 (every out-of-batch look) from experiments/*/summary.json in 0.2 s, stdlib; tests tests/test_paper_tables.py (7) check it reproduces the counts, cycles and worst misses 7f, 7g and 7h logged.
  • Computed for the section, after every milestone had reported (descriptive, no hypothesis): Wilson 95% on each hit count; pooled fresh-pool hit rate of 7f's frozen θ policies on 7g and 7h, 18/24 = 0.75, with a bootstrap over the 8 (pool, set) clusters, since a set's three policies share one fresh pool; the paired lopo5 cycle difference θ − U per fold: mean −4.50, cheaper 14, dearer 4, tied 2, exact sign p = 0.0309, bootstrap over the 4 sets −8.50 to +0.25; both rules meet on 18 folds, each alone on 1.
  • Reading: the paper's claim is now sized. The saving replicates (two blind looks, each 9 of 12) and the threshold rule beats uniform fold by fold, but with four parameter sets the across-chemistry interval still spans zero; adding sets helps the paper more than adding pools. The worst miss on a fresh pool is 1.58 times the target (Chen2020, the most permissive 7f policy, missed on both fresh pools).
  • Caveats: the bootstraps resample 8 and 4 clusters, too few for a percentile interval to be more than indicative; only 4 of lopo5's 20 folds are blind; all caveats of 7f to 7h carry over.
  • Output: paper/results.md, paper/tables.txt, paper/tables.json; tests tests/test_paper_tables.py.

2026-11-19 · Milestone 7h outcome: on 64 more designs no step had simulated, 7f's frozen threshold policies meet the tail target in 9 of 12 for the third time running (now at 39.3 DFN cycles per design, 21% saved against all-50), and 7g's refit policies meet 4 of 4 at 37.8. The new batch-relative threshold (R50) meets 4 of 4 at 40.6 cycles, the absolute ones 3 of 4 at 40.0; over all five pools by leave-one-pool-out, every drift-score rule meets 16 to 19 of 20 folds at 42 to 44 cycles, the uniform rule 19 of 20 at 48.0. The relative threshold does not make the flagged share more stable (H287 refuted). H285, H288 and H289 supported, H286 inconclusive (4 of 4 met, at 40.6 cycles against its 40 line), H287 refuted

  • Bench: 64 DFN runs to cycle 100 through 7g's runner, about 9 minutes on 3 workers; 62 ok first time, 2 (Ai2020 j = 50, 52) killed for memory and re-run with 1 worker, both ok (the failed attempts stay in bench.jsonl as ok: false). Tests ran before rows and report; both run once; run.py unchanged after the plan commit (figure.py added after the report).
  • Fresh pool (16 designs per set): all-50 q75 0.039, 0.045, 0.055, 0.020; all-10 q75 1.6 to 3.6 times higher. Median S<sub>C</sub> on 7h sits back near the 104's on every set (Ai2020 0.098 against 0.057 to 0.077, and 0.120 on 7g; Chen2020 0.026 against 0.025 to 0.029, and 0.047 on 7g): the scale jump 7g saw did not recur.
  • H285 supported (9 of 12, 39.3 cycles): misses Chen2020 from 5zk (0.089 against 0.056 at 25 cycles), OKane2022 from 5zz (0.072 against 0.068), NCA_Kim2011 from 5zk (0.031 against 0.025, 22.5 cycles). Chen2020 5zk and NCA_Kim2011 5zk also missed on 7g: the two most permissive 7f policies miss every time.
  • H286 inconclusive: R50 refit4 meets 4 of 4 at 40.6 cycles (19% saved), 0.6 over its line. Its margins fell back to 1.00 on two sets (no grid value met all four inner folds), and it flags 88% to 97% of training designs on three sets.
  • H287 refuted: mean |flagged share on 7h − on training| 0.095 for R50 against 0.069 for θ50. With the scale steady on 7h there was little drift to absorb, and the median of 16 designs moves the relative cut by itself.
  • H288 supported (3 against 3): with four training pools the free-K1 rule picks K1 = 50 on every set anyway, so θ50 and θ-tight are the same policy here (identical rows).
  • H289 supported: R50 meets 18 of 20 lopo5 folds at 42.1 cycles (16% saved). Absolute threshold 19 of 20 at 43.5 (13%), fraction 16 at 43.2, uniform 19 at 48.0 (4%).
  • Reading: the triage saving has now replicated on two fresh batches nothing had simulated: 9 of 12 frozen policies met each time, at 17% (7g) and 21% (7h) fewer DFN cycles, and the same misses recur on the two most permissive policies. With more pools to set the margin, the extension length settles at 50 by itself and the threshold rules meet 19 of 20 held-out pools at 13% saved, where a uniform run length meets 19 at 4%: about three times the saving at the same hit rate. The batch-relative threshold is not needed (it does no better and needs a batch); the absolute threshold on the drift score stays the paper's rule. For the paper: report the three looks (7f reused, 7g and 7h fresh) and lopo5 as the headline, with the honest saving a seventh to a fifth of the DFN budget. Next: write the results section (5zk to 7h).
  • Caveats: 16 designs per set on 7h (q75 is the 4th largest), the 4 refit4 folds are 4 tests, lopo5's 16 folds holding out an earlier pool were seen before (only the 4 holding out 7h are blind); R50's design was informed by 7g's misses; one law form and κ (25.3); OKane2022's plating parameters on every set; one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/fresh7h/results.txt, summary.json, rows.json, bench.jsonl, fresh7h.svg; tests tests/test_fresh7h.py.

2026-11-19 · Milestone 7h (a fifth fresh pool and a scale-free threshold): 7g found 7f's frozen triage rules met the tail target in 9 of 12 policies on 32 never-simulated designs, but the absolute drift threshold over-flagged where a fresh pool's S<sub>C</sub> ran higher, and two misses came from a 40-cycle extension. Does a threshold relative to the batch's own median S<sub>C</sub>, with the extension fixed at 50 cycles, hold the target on 64 more designs nothing has simulated? (plan, written and committed before the fresh bench ran; H285 to H289 are this entry's)

  • Question: 7g's next steps: a K1 = 50-only rule and a design-ranked threshold to remove the scale drift, scored on fresh designs.
  • Bench, fixed now (experiments/fresh7h/run.py bench): 16 designs per set from the same 64-design pools, excluding every design 5z, 5zy, 5zz and 7g picked, by random.Random(5291) (picks listed by jobs() while writing the code: j = 8, 9, 10, 34, 36, 43, 46, 47, 48, 51, 53, 54, 55, 57, 61, 62 for Chen2020 and OKane2022; 5, 8, 9, 10, 22, 26, 33, 37, 43, 46, 48, 50, 51, 54, 58, 62 for NCA_Kim2011; 8, 9, 10, 22, 25, 26, 33, 37, 43, 46, 48, 50, 51, 52, 60, 61 for Ai2020; disjoint from the 136, tested), run to cycle 100 with 5zk's x-resolved child through 7g's runner, unchanged, PyBaMM 26.10.1.1. Rows as 7g (S<sub>C</sub> correction fitted on the set's 104 designs only).
  • Rules (cell 000; target 1.25 × the scored pool's own all-50 q75): R50 (primary, new): K1 = 50, flag a design when S<sub>C</sub> ≥ ρ × the median S<sub>C</sub> of the batch it is triaged in (training: each design against its own pool's median; candidates ρ = every training ratio and +∞); θ50: 7f's absolute threshold with K1 = 50 only; θ-tight (K1 free), F-tight, U-tight as 7f. refit4: each picked on the four earlier pools of a set (5zk, 5zy, 5zz, 7g), margin t′ the most permissive grid value (1.25 to 1.00) whose four inner folds (pick on three pools, score on the fourth) all meet, else 1.00; applied once to the 7h pool (4 folds). frozen: 7f's 12 nested θ-tight policies and 7g's 4 refit ones, unchanged. lopo5 (20 folds): each of a set's five pools held out in turn, margin from the other four.
  • H285 (second replication): at least 9 of 7f's 12 frozen θ-tight policies meet on the 7h pool. Refuted if 6 or fewer.
  • H286 (R50 holds and saves): refit4 R50 meets on at least 3 of 4 sets at a mean of at most 40 DFN cycles per design. Refuted if 1 or none, or above 45.
  • H287 (the mechanism: scale-free flagging): the mean over sets of |flagged share on 7h − flagged share on training| is smaller for R50 than for θ50. Refuted if larger.
  • H288 (K1 = 50 is enough): refit4 θ50 meets on at least as many sets as refit4 θ-tight. Refuted if fewer.
  • H289 (R50 out of batch, all pools): R50 meets at least 15 of 20 lopo5 folds. Refuted if 11 or fewer.
  • Already seen: everything through 7g on the 136 designs (so R50's design was informed by 7g's misses; only the 7h pool is blind, and lopo5's 16 folds holding out an earlier pool are not). Not seen: any DFN output for the 64 fresh designs.
  • Risks named now: 16 designs per set (q75 is the 4th largest); the 4 refit4 folds are 4 tests; the relative rule needs a batch (it cannot score a lone design, which the absolute rule can); median of a small pool is itself noisy; 7h's S<sub>C</sub> is fitted on all 104 while the 104's own is leave-one-out (the scale difference R50 is meant to absorb); one law form and κ (25.3); OKane2022's plating parameters on every set; one PyBaMM version; modelled fade only.

2026-11-19 · Milestone 7g outcome: on 32 designs no step had simulated, 7f's frozen triage rules still meet the tail target in 9 of 12 policies (threshold on the drift score, and flag fraction, both), at 41.7 and 40.5 DFN cycles per design against 50 for running every design to cycle 50: 17% and 19% saved, against 20% in 7f. Widening the flagged fraction alone (F+Δ) collapses from 6 of 12 to 5. Refit on all three earlier pools, the threshold rule meets 3 of 4 sets at 41.2 cycles; the uniform rule meets 4 of 4 at 47.5 (5% saved). H281 and H283 supported, H282 and H284 inconclusive (both just over their 40-cycle line)

  • Bench: 32 DFN runs to cycle 100, about 6 minutes on 3 workers, all 32 ok first time (6.8 MB, committed). Tests ran before rows and report; both run once; nothing in the plan's code changed after the plan commit (posthoc and figure.py added after the report).
  • Fresh pools (8 designs each): all-50 q75 0.038, 0.053, 0.050, 0.029 (Ai2020, Chen2020, OKane2022, NCA_Kim2011); all-10 q75 0.085, 0.133, 0.095, 0.087, so the ten-cycle line alone is 2.2 to 3.0 times worse at the tail here, as on the 104.
  • H281 supported (9 of 12): misses Ai2020 from 5zz (K1 = 40, q75 0.055 against 0.048), Chen2020 from 5zk (0.070 against 0.066, 35 cycles), NCA_Kim2011 from 5zk (0.037 against 0.036, 20 cycles). Two of the three misses are policies that also missed their own held-out pool in 7f (Ai2020 5zz, NCA_Kim2011 5zk); 8 of the 9 that met in 7f meet here, and 1 of the 3 that missed in 7f (OKane2022 5zz) meets. The worst miss is 1.15 times the target.
  • H282 inconclusive (3 of 4 at 41.2 cycles): refit θ-tight misses Ai2020 (the 40-cycle extension again), meets Chen2020 (40), OKane2022 (45), NCA_Kim2011 (40). Inner folds found no margin meeting all three on Ai2020 and OKane2022.
  • H283 supported (9 against 9): frozen F-tight also meets 9 of 12, at 40.5 cycles.
  • H284 inconclusive (41.7 cycles, 16.6% saved): between the 40 (supported) and 45 (refuted) lines.
  • Reported: frozen F+Δ 5 of 12 at 34.0; refit F-tight 3 of 4 at 41.6, F+Δ 2 of 4 at 33.1; at zero margin the refit rules meet 0 (threshold), 1 (fraction) and 2 (uniform) of 4: the margin is still what makes the rule hold.
  • Post hoc, descriptive (after the report, posthoc.txt): the fresh pools' S<sub>C</sub> runs higher than the 104's leave-one-out S<sub>C</sub> on Ai2020 (median 0.121 against 0.074) and Chen2020 (0.056 against 0.028), so an absolute threshold flags more fresh designs than it was set to (all 8 on Ai2020 for two policies, 50 cycles each): the threshold's saving depends on the score's scale holding across batches, and here it did not. In hindsight on each fresh pool the cheapest threshold policy costs 35.0, 32.5, 25.0, 30.0 cycles and the cheapest uniform 50, 40, 50, 50, so the forward rules keep about half of what was there to keep.
  • Reading: the out-of-batch numbers of 7f replicate on designs nothing had seen: a margin set by nested leave-one-pool-out holds the tail target on about three in four batches and saves a sixth to a fifth of the DFN budget, where a uniform run length saves nothing to 5%. The misses are near-misses (worst 1.15 times the target) and two have one cause, a 40-cycle extension that is too short on Ai2020, which suggests fixing K1 = 50 and tuning only who is flagged. The threshold and the fraction remain tied; the fraction is immune to the score's scale drift, the threshold needs no batch. For the paper: 20% (7f) and 17 to 19% (7g) are the honest savings, with 9 of 12 met both times. Next: the paper's results section (5zk to 7g); a K1 = 50-only rule; a design-ranked rather than absolute threshold (a quantile of the training S<sub>C</sub>) to remove the scale drift.
  • Caveats: 8 designs per fresh pool, so a q75 is one design and the 12 frozen policies are effectively 4 tests (3 per set share one pool); S<sub>C</sub> on the fresh pool comes from a fit on all 104, the 104's own from leave-one-out, and the scales differ (post hoc); one law form and κ (25.3); OKane2022's plating parameters on every set; one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/fresh7g/results.txt, summary.json, rows.json, bench.jsonl, posthoc.txt, fresh7g.svg; tests tests/test_fresh7g.py.

2026-11-19 · Milestone 7g (a fourth fresh pool): 7f's nested-margin triage rules met the held-out tail target in 9 (drift threshold) and 10 (flag fraction) of 12 folds at 40 DFN cycles per design, but every fold reused the three pools 5zk, 5zy and 5zz. Do those rules, frozen, still meet the target on 32 designs no step has simulated, and does the threshold rule still save a fifth of the DFN budget there? (plan, written and committed before the fresh bench ran; H281 to H284 are this entry's)

  • Question: 7f's next step: the fourth fresh pool (new DFN runs to cycle 99 on 8 designs per set) to score the nested rules once more with no reuse.
  • Bench, fixed now (experiments/fresh7g/run.py bench): 8 designs per set from the same 64-design pools as 5zy and 5zz, excluding every design 5z, 5zy and 5zz picked, by random.Random(5281) (picks listed by jobs() while writing the code: j = 4, 24, 25, 27, 35, 39, 41, 49 for Chen2020 and OKane2022; 4, 16, 17, 29, 34, 38, 44, 63 for NCA_Kim2011 and Ai2020; disjoint from the 104, tested), run to cycle 100 with 5zk's x-resolved child (depth/run.py child), unchanged, PyBaMM 26.10.1.1.
  • Rows (rows, stdlib): per fresh design, 7b's line error e<sub>k</sub> at k = 10, 15, 20, 30, 40, 50 and 7c's drift inputs (O1 to O3, m), cells 000 and 111, by the same _job functions. S<sub>C</sub> = |m̂<sub>C</sub> − 1| with 7c's correction (observable with the largest |Spearman| with m, its least-squares line) fitted on the set's 104 earlier designs only: no fresh design informs any fresh design's score (stricter than the 104's own leave-one-out S<sub>C</sub>).
  • Rules, scored on the fresh pool of each set at 1.25 × that pool's own all-50 q75 (cell 000, 8 designs, so q75 is the second largest): frozen = each of 7f's 12 nested-margin policies (set, held-out pool) for θ-tight, F-tight, U-tight and F+Δ, applied unchanged (tested to reproduce 7f's 12 θ-tight folds); refit = each rule picked on all three earlier pools of a set, its margin the most permissive grid value whose three inner folds (pick on two pools, score on the third) all meet, else the most conservative (4 folds); zero = refit at margin 1.25 (reported). Realised cost: the fresh pool's DFN cycles per design.
  • H281 (the frozen threshold rule transfers): of 7f's 12 frozen θ-tight policies, at least 9 meet the fresh pool's target. Refuted if 6 or fewer.
  • H282 (refit on three pools): refit θ-tight meets on at least 3 of 4 sets at a mean of at most 40 cycles per design. Refuted if it meets on 1 or none, or costs more than 45.
  • H283 (threshold against fraction, again): frozen θ-tight meets at least as many of the 12 as frozen F-tight. Refuted if fewer.
  • H284 (the saving survives): frozen θ-tight's mean realised cycles on the fresh pools is at most 40 (at least 20% saved against U50). Refuted if above 45 (under 10% saved).
  • Already seen: everything 5zk to 7f report on the 104 designs. Not seen: any DFN output for the 32 fresh designs (only their indices and design vectors).
  • Risks named now: 8 designs per set, so a fresh q75 is one design and the 12 frozen policies of a set share one fresh pool (3 per set, not independent; the 12 are effectively 4 tests); the threshold rule's absolute θ was set on S<sub>C</sub> values from a leave-one-out fit, while the fresh S<sub>C</sub> comes from a fit on all 104, so the two scales may differ slightly; one law form and κ (25.3); OKane2022's plating parameters on every set; one PyBaMM version; modelled fade only.

2026-11-19 · Milestone 7f outcome: a margin chosen by nested leave-one-pool-out turns the triage rule from 4 of 12 held-out pools met to 9 (absolute threshold on the drift score) or 10 (flag fraction), at 40.0 DFN cycles per design against 50 for running every design to cycle 50, a 20% saving. The uniform rule with the same margin choice always lands on 50 cycles (12 of 12, nothing saved), and adding a margin to the flag fraction alone (F+Δ) meets only 6. H277 and H280 supported (H280 at its 20% line), H279 refuted (threshold 9 against fraction 10), H278 inconclusive (threshold misses 3 more folds than uniform but costs 10 fewer cycles)

  • Analysis: stdlib, 0.2 s, tests run before the report (tests/test_margin7f.py; zero-margin U-tight and F-tight reproduce 7e's 12 transfer folds), report run once; run.py unchanged after the plan except the H278 refutation clause, corrected to the plan's wording before the report ran.
  • Zero margin (reproduces 7e and adds the threshold rule): threshold 3 of 12 met at 26.5 cycles, fraction 4 at 27.3, uniform 7 at 41.7.
  • Nested margin: threshold 9 of 12 at 40.0 cycles (misses Ai2020 5zz at 1.08 times the target, OKane2022 5zz at 1.16, NCA_Kim2011 5zk at 1.01); fraction 10 at 40.0 (misses Ai2020 5zk at 1.40, 5zz at 1.08); F+Δ 6 at 34.2 (the extension length K1 picked at zero margin is too short on most folds, and a larger f cannot fix that); uniform 12 at 50.0 (every fold's margin ends at U50).
  • H277 supported (9 of 12). H278 inconclusive (9 against 12 met; 40.0 against 50.0 cycles): the plan's two refutation clauses both need the threshold rule to cost no less, and it costs less. H279 refuted (9 against 10). H280 supported: best rule meeting at least 9 is threshold or fraction (tied at 39.97 cycles per design), 20.07% saved against U50, on the plan's 20% line.
  • Inner folds: 5 of 12 outer folds found no t′ on the grid that met both inner folds for the threshold rule (fell back to t′ = 1.00), 3 of 12 for the fraction rule, 0 for uniform. The grid's most conservative point is still too permissive on OKane2022 for the threshold rule.
  • Post hoc, descriptive (after the report): the threshold rule's worst held-out miss is 1.16 times the target, the fraction rule's 1.40; uniform's worst held-out q75 is 0.80 times the target, so U50 overshoots the accuracy it was asked for by 20% on every fold. The tie at 39.97 cycles is a coincidence of two different fold-by-fold profiles (per-fold costs differ on 6 folds).
  • Reading: with a margin set out of batch, triage keeps a fifth of the DFN budget and meets the held-out tail target about as often as one would accept from a 12-fold check (9 or 10 of 12), while the uniform rule, given the same margin procedure, cannot save anything: no run length shorter than 50 cycles holds across pools. The in-sample savings of 7d and 7e (33% to 61%) shrink to 20% out of batch, which is the honest number for the paper. Threshold against fraction is not settled (one fold apart); the threshold rule has the attraction that it needs no batch to rank against, so it applies to one design at a time in a sequential search. Next: the fourth fresh pool (new DFN runs to cycle 99 on 8 designs per set) to score the nested rules once more with no reuse; the paper's results section (5zk to 7f).
  • Caveats: 8 to 12 designs per pool, inner folds pick on 8 to 12 designs; margin grids coarse (t′ to 1.00, Δ to 0.50); S<sub>C</sub> is 7c's leave-one-out correction fitted on all pools' drift, so pools share information (flatters both triage rules); one law form and κ (25.3); OKane2022's plating parameters on every set; one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/margin7f/results.txt, summary.json, margin7f.svg; tests tests/test_margin7f.py.

2026-11-19 · Milestone 7f (a triage rule with an out-of-batch margin): 7e's triage policy, picked on two design pools, met the third pool's tail target in 4 of 12 folds. Does a margin chosen by nested leave-one-pool-out, or an absolute flag threshold on the drift score instead of a flag fraction, bring the held-out hit rate up while keeping the DFN cycles saved? (plan, written and committed before any rule below was applied to a held-out pool; H277 to H280 are this entry's)

  • Question: 7e's next step: set the triage rule's margin out of batch, by leave-one-pool-out, and score it by held-out target misses and cycles together.
  • Method, fixed now (experiments/margin7f/run.py report; stdlib, no new simulation, reads 7e's join of 7d's and 7b's rows through frontier7e/run.py's load, cell 000, the 104 designs, target 1.25 × the pool's own all-50 q75 as 7e's H276). Four rules, each a function of training designs and a margin m: - U-tight: the cheapest uniform U(k) whose training q75 is at most t′ × training q75(U50); m = t′ in {1.25, 1.20, 1.15, 1.10, 1.05, 1.00} (most to least permissive). - F-tight: the cheapest 7e triage policy T(K1, f, S<sub>C</sub>) meeting t′ on training, same grid; applied to the held-out pool as the fraction f of that pool ranked by S<sub>C</sub> (7e's transfer). - F+Δ: the T(K1, f) picked at t′ = 1.25, applied with f + Δ (clamped at 1), Δ in {0, 0.05, ..., 0.50}. - θ-tight (primary): for K1 in {15, 20, 30, 40, 50} and an absolute threshold θ on S<sub>C</sub> = |m̂<sub>C</sub> − 1| (candidates: each training design's S<sub>C</sub>, and +∞ for flag none), flag every design with S<sub>C</sub> ≥ θ; the cheapest (K1, θ) meeting t′ on training (training cost 10 + (K1 − 10) × flagged share; ties to the larger θ, then smaller K1), applied unchanged to the held-out pool. - No policy meeting t′ on training means U50. Margin choice by nested leave-one-pool-out: in each of 7e's 12 outer folds (set, held-out pool), the two training pools A, B give two inner folds (pick on A, score on B at 1.25 × B's all-50 q75, and the reverse); m is the most permissive grid value whose two inner folds both meet, or the most conservative if none does. The rule at that m is then picked on A ∪ B and applied to the held-out pool. Score per fold: met (held-out q75 at or below the target) and the held-out pool's realised DFN cycles per design (10 + (K1 − 10) × the share of that pool flagged; k for U(k)). Reference rules: U50 (always meets, 50 cycles) and each rule at zero margin (U-tight and F-tight at m = 1.25 reproduce 7e's transfer, tested).
  • H277 (the primary rule hits): θ-tight with the nested margin meets the held-out target in at least 9 of 12 folds. Refuted if 6 or fewer.
  • H278 (it pays against uniform): θ-tight misses no more folds than U-tight with its nested margin and costs fewer mean held-out cycles over the 12 folds. Refuted if it misses more folds and costs no less, or costs more and misses no fewer.
  • H279 (threshold beats fraction): θ-tight meets more folds than F-tight (both nested). Refuted if fewer.
  • H280 (the margin is worth its cycles against always-50): the best of the four nested rules that meets at least 9 of 12 folds saves at least 20% of DFN cycles against U50 averaged over the 12 folds. Refuted if no rule meets 9, or if every one that does saves less than 10%.
  • Already seen: 7e's zero-margin transfer (S<sub>C</sub> fraction 4 of 12, uniform 7 of 12) and its post hoc note that held-out targets vary fivefold across pools of one set. Not seen: any margin other than zero, any threshold rule, any inner fold.
  • Risks named now: 8 to 12 designs per pool, so each inner fold picks on one pool of 8 to 12 designs and a held-out q75 is one or two designs; the margin grids are coarse and the most conservative t′ = 1.00 may still miss (the training q75 of U50 is not the held-out one); S<sub>C</sub> is 7c's leave-one-out correction fitted on all pools' drift (shared information across pools flatters any S<sub>C</sub> rule); a fresh fourth pool, which 7e also asked for, needs new DFN runs to cycle 99 and is not in this step.

2026-11-19 · Milestone 7e outcome: in hindsight, drift-score triage is cheaper than any uniform run length at almost every tail target (strictly cheaper at 14, 18, 21 and 21 of 21 targets; mean DFN cycles saved against all-50 55%, 61%, 33%, 46% against uniform's 36%, 39%, 27%, 18% and random triage's 48%, 52%, 30%, 31%). A 30-cycle extension is not enough at 7d's target on three of four sets (Chen2020 needs U30 at 30 cycles against 16 for 15% extended to 50; OKane2022 and NCA_Kim2011 cannot meet it at all with K1 ≤ 30). But the policy does not transfer: picked on two design pools and applied to the third, it meets the held-out target in 4 of 12 folds, against 7 of 12 for a uniform run length picked the same way. H273 and H275 supported, H274 and H276 refuted

  • Analysis: stdlib, 6 s, tests run before the report, report run once; run.py unchanged after the plan. Reproduces 7d: the K1 = 50 slice at t = 1.25 gives 7d's S<sub>C</sub> f* on all four sets (tested).
  • H273 supported (4 of 4): T(S<sub>C</sub>) strictly cheaper than U at 14, 18, 21, 21 of 21 targets (Ai2020, Chen2020, OKane2022, NCA_Kim2011).
  • H274 refuted (1 of 4 at or below; more on 3): at t = 1.25, cheapest T(S<sub>C</sub>) with K1 ≤ 30 against K1 = 50: 28.0 against 32.0 (Ai2020, 30@0.90), 30.0 against 16.0 (Chen2020), unmet against 48.0 (OKane2022), unmet against 28.0 (NCA_Kim2011). The uniform q75 at k = 30 is still 1.3 to 1.8 times the k = 50 one (0.042, 0.071, 0.063, 0.040 against 0.027, 0.057, 0.040, 0.022): on three sets the 30-cycle line is too short to reach 1.25 times all-50 even for every design.
  • H275 supported (4 of 4): mean saved T(S<sub>C</sub>) against T(random) 55% and 48%, 61% and 52%, 33% and 30%, 46% and 31%; oracle 70%, 70%, 41%, 49%.
  • H276 refuted (4 of 12 folds met; uniform 7 of 12): S<sub>C</sub> met on Ai2020 5zy, Chen2020 5zz, OKane2022 5zy, NCA_Kim2011 5zk. Three folds where uniform met and S<sub>C</sub> missed: Ai2020 5zk and 5zz, NCA_Kim2011 5zz (q75 0.060 against target 0.031 with half the pool extended to 50: a missed design).
  • Post hoc, descriptive (after the report): over the 12 folds the transferred S<sub>C</sub> policies cost 27.3 DFN cycles per design on average against 41.7 for the transferred uniform ones, and their held-out q75 averages 1.18 times the target against 0.97. Held-out targets vary fivefold across pools of one set (Ai2020 0.017 to 0.058), so the q75 of 8 designs (the second largest) is a noisy target in its own right.
  • Reading: the frontier says triage is the right shape for a design search's fidelity budget, and that the extension has to be long: 30 cycles do not buy 50-cycle tail accuracy on these cells, so the gain comes from running few designs long, not many designs a little longer. But the savings 7d and this milestone report are in hindsight: the flagged fraction that meets the target on one batch of designs undershoots on the next, more often than a uniform run length does, because a triage policy is betting on which few designs carry the tail and a small batch's tail is one or two designs. A usable rule needs a margin set on held-out batches (a larger f than the in-sample one, or a fixed flag threshold on S<sub>C</sub> rather than a fraction), scored by out-of-batch target misses as well as cycles. Next: that rule, with the margin chosen by leave-one-pool-out and checked on a fourth fresh pool; and the paper's results section (5zk to 7e).
  • Caveats: 24 to 28 designs per set and 8 to 12 per pool; costs are least over many policies in hindsight within the set (the in-sample curves), which H276 shows overstates what a forward choice keeps; S<sub>C</sub> is 7c's leave-one-out correction fitted on all pools' 99-cycle drift, so even the transfer folds share information across pools (it flatters S<sub>C</sub>, so the refutation stands); e<sub>K1</sub> from 7b's lines; one law form and κ (25.3); OKane2022's plating parameters on every set; one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/frontier7e/results.txt, summary.json, frontier7e.svg; tests tests/test_frontier7e.py.

2026-11-19 · Milestone 7e (the triage frontier): how long should the flagged designs run, and how many DFN cycles does triage save across a range of tail-error targets rather than at one? (plan, written and committed before any policy below was computed with an extension other than 50 cycles or a target other than 1.25; H273 to H276 are this entry's)

  • Question: 7d scored one policy family (flag a fraction f by 7c's drift score S<sub>C</sub>, extend those to cycle 50) at one target (1.25 times the all-50 q75). Its next step: whether the triage holds with a 30-cycle extension and a tighter target, scored as a curve of cycles saved against target.
  • Method, fixed now (experiments/frontier7e/run.py, report; stdlib, no new simulation, reads 7d's triage7d/rows.json joined with 7b's lawfloor/rows.json for e at k = 15, 20, 30, 40, 50): policies on each set, cell 000 primary. Uniform U(k): every design gets the k-cycle line, k in {10, 15, 20, 30, 40, 50}, cost k. Triage T(K1, f, score): the round(f n) designs with the largest score get the K1-cycle line, the rest the ten-cycle line, K1 in {15, 20, 30, 40, 50}, f on 7d's 0.05 grid, cost 10 + (K1 − 10) f per design. Scores S<sub>C</sub> (primary) and random (expected q75 over 2,000 draws, random.Random(79), as 7d); oracle by the design's own gain e<sub>10</sub> − e<sub>K1</sub> as a ceiling. Targets t × q75(U(50)), t in {1.00, 1.05, ..., 2.00} (21 targets). For each family, the cost to meet a target is the least cost of any of its policies whose q75 is at or below it (hindsight within the set, as 7d's f*); unmet counts as 50 cycles. Saved = 1 − cost/50; a family's curve is saved against t, and its score the mean over the 21 targets.
  • H273 (triage beats uniform): T(S<sub>C</sub>) strictly cheaper than U at at least 11 of 21 targets on at least 3 of 4 sets. Refuted if on 1 or none.
  • H274 (a 30-cycle extension is enough at 7d's target): at t = 1.25, the cheapest T(S<sub>C</sub>) policy with K1 ≤ 30 costs no more than the cheapest with K1 = 50 on at least 3 of 4 sets. Refuted if it costs more on at least 3.
  • H275 (better than random over the whole curve): mean saved of T(S<sub>C</sub>) above T(random)'s on at least 3 of 4 sets. Refuted if at or below on at least 3.
  • H276 (the choice transfers across pools): leave one pool out (5zk, 5zy, 5zz; 12 set-pool folds): pick the cheapest T(S<sub>C</sub>) policy (K1, f) meeting t = 1.25 on the other two pools' designs (S<sub>C</sub> ranks within the training designs and, for the held-out pool, within that pool), apply it to the held-out pool, and score it against 1.25 times that pool's all-50 q75. Supported if met in at least 8 of 12 folds; refuted if in 4 or fewer. Uniform U(k) picked the same way reported alongside.
  • Already seen: e at k = 10 and 50 per design and 7d's q75 curves for K1 = 50 at t = 1.25; 7b's set medians at every k. Not seen: any triage policy with K1 < 50, any target other than 1.25, any per-pool policy.
  • Risks named now: 24 to 28 designs per set (8 to 12 per pool, so a held-out q75 is one or two designs); taking the least cost over many policies in hindsight flatters triage more than uniform (more policies to choose from), which H276 partly checks; e<sub>K1</sub> is not monotone in K1 for some designs (7b), so a shorter extension can beat a longer one by chance; one law form and κ.

2026-11-19 · Milestone 7d outcome: on two of four parameter sets, simulating only the designs a ten-cycle drift score flags keeps the 50-cycle forecast's tail accuracy for about half the DFN cycles. With the real ten-cycle forecast, the upper-quartile cycle-99 lithium-loss error falls from 11.4% to within 1.25 times the all-50 figure (5.7%) once 15% of Chen2020's designs are extended (68% of the all-50 cycles saved; random flags need 50%, saving 40%), and on NCA_Kim2011 once 45% are (44% saved against random's 20%). On OKane2022 no score saves anything (95% must be extended, as for random flags), and on Ai2020 it saves 36% against random's 24%. With every input measured, the cycle-2 plating depth alone beats the full correction on LG M50 (20% extended against 60%). H269, H271 and H272 supported, H270 inconclusive

  • Analysis: stdlib, 2 s, tests run before the report, report run once; run.py unchanged after the plan. Reproduces 7b and 7c: each design's ten-cycle error equals 7c's line error on all 104 designs and both cells (to 12 places, tested); the all-10 and all-50 policies are 7b's k = 10 and k = 50 lines.
  • H269 supported (3 of 4): q75 e<sub>000</sub> at f = 0.25, S<sub>C</sub> against random: Ai2020 0.043 and 0.043 (S<sub>C</sub> marginally worse, 0.0434 against 0.0429), Chen2020 0.066 and 0.087, OKane2022 0.078 and 0.082, NCA_Kim2011 0.060 and 0.066; oracle 0.032, 0.066, 0.070, 0.042.
  • H270 inconclusive (2 of 4 at f* ≤ 0.5, 1 above 0.75): S<sub>C</sub>'s f* 0.55, 0.15, 0.95, 0.45 (cycles saved 36%, 68%, 4%, 44%), against targets 0.034, 0.071, 0.050, 0.028 (all-10 q75 0.045, 0.114, 0.100, 0.075; all-50 0.027, 0.057, 0.040, 0.022).
  • H271 supported (3 of 4): random flags' f* 0.70, 0.50, 0.95, 0.75 (24%, 40%, 4%, 20% saved); OKane2022 a tie. Oracle f* 0.25, 0.10, 0.85, 0.40 (60%, 72%, 12%, 48%), so S<sub>C</sub> is within 0.05 of the oracle on Chen2020 and NCA_Kim2011.
  • H272 supported: cell 111 f* on Chen2020 and OKane2022, S<sub>1</sub> 0.20 and 0.20 (64% saved), S<sub>C</sub> 0.60 and 0.60 (32%), random 0.50 and 0.45, oracle 0.10 and 0.10. For the real forecast (cell 000) S<sub>1</sub> is worse than S<sub>C</sub> on three sets (f* 0.50, 0.30, 1.00, 0.80).
  • Reported: the q75 curves are not monotone in f: extending a design does not always help (e<sub>50</sub> > e<sub>10</sub> on 4, 3, 3 and 1 designs of the four sets, cell 000), so on Chen2020 S<sub>C</sub>'s q75 sits at 0.066 from f = 0.2 to 0.9 and only reaches the all-50 0.057 at f = 1; on Ai2020 the q75 at f = 0.9 (0.022) is below the all-50 one (0.027).
  • Reading: a design search does not have to pick between ten cycles for every candidate and fifty. 7c's drift score, known at cycle 10, ranks which designs' ten-cycle forecasts will be badly wrong well enough to buy most of the 50-cycle tail accuracy with a fraction of the cycles on Chen2020 and NCA_Kim2011, and it does no worse than random elsewhere. Where it fails (OKane2022), the oracle fails too (85% extended): the tail there is spread over most designs, so there is nothing to triage. The score that flags best depends on what the forecast's error is made of: with measured inputs the error is the law's drift and the plating depth alone flags it (H272); with the real forecast the inputs' error adds in, and the full correction, which picks its observable per fold, does better. Next: the paper's results section from 5zk to 7d (error budget, the law floor, the drift and this triage as its four tables); then whether the triage holds with a 30-cycle extension and a tighter target, scored as a curve of cycles saved against target rather than one point.
  • Caveats: 24 to 28 designs per set, so q75 is one design's error and f* moves by whole designs; one target (1.25 times all-50) and a 0.05 grid; the flags rank within a set, a batch decision a live search makes only once its ten-cycle runs are in; S<sub>C</sub> is 7c's leave-one-out correction, so its fit used the other designs' 99-cycle drift; O1 is a model internal; one law form and κ (25.3); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/triage7d/results.txt, summary.json, rows.json, triage7d.svg; tests tests/test_triage7d.py.

2026-11-19 · Milestone 7d (flag and extend): if only the designs a ten-cycle score flags are simulated to cycle 50, how much of the 50-cycle forecast's tail accuracy does a design search keep, and how many DFN cycles does it save? (plan, written and committed before any triage policy below was computed on these designs; H269 to H272 are this entry's)

  • Question: 7c found that cycle-2 plating depth and the bend of lithium loss predict which designs' fade-law rate drifts, and post hoc that a correction built on them halves the upper-quartile ten-cycle error, while 7b found that a 50-cycle line removes most of the real forecast's error (cell 000 set medians 0.025, 0.056, 0.067, 0.040 at k = 10 against 0.010, 0.027, 0.021, 0.014 at k = 50). 7c's next step: a decision rule that sends only flagged designs to a longer simulation, scored on DFN cycles saved at a tail-error target.
  • Method, fixed now (experiments/triage7d/run.py, rows, report; stdlib, no new simulation): join 7b's lawfloor/rows.json (e at k = 10 and 50, cells 000 and 111) and 7c's drift7c/rows.json (m̂<sub>C</sub>, O1) on (cond, j, pool), all 104 designs. Each design's forecast costs k DFN cycles. Policy F(f, score): within a set, the fraction f of designs with the largest score get the 50-cycle line (e<sub>50</sub>), the rest keep the ten-cycle line (e<sub>10</sub>); cost per design 10 + 40 f. Scores, all known at cycle 10: S<sub>C</sub> = |m̂<sub>C</sub> − 1| (7c's leave-one-out drift correction for that cell, primary), S<sub>1</sub> = |O1 − median O1 of the set's other designs|. Controls: R(f), random flags (expected quantile over 2,000 draws, random.Random(79)); O(f), oracle flags by the design's own gain e<sub>10</sub> − e<sub>50</sub> (a ceiling). f on the grid 0, 0.05, ..., 1 (flag count round(f n)). Tail metric: q75 of e over the set (7c's quant, index int(0.75 n)); target per set and cell: 1.25 times the q75 of the all-50 policy. f* is the smallest grid f whose q75 meets the target; cycles saved = 1 − (10 + 40 f*)/50. Primary cell 000 (the real forecast); cell 111 reported with the same rule.
  • H269 (the score finds the tail): at f = 0.25, F(S<sub>C</sub>)'s q75 e<sub>000</sub> below R(0.25)'s on at least 3 of 4 sets. Refuted if on 1 or none.
  • H270 (it saves cycles): F(S<sub>C</sub>)'s f* ≤ 0.5 (at least 40% of the all-50 cycles saved) on at least 3 of 4 sets, cell 000. Refuted if f* > 0.75 on at least 3.
  • H271 (better than random): F(S<sub>C</sub>)'s f* below R's f* on at least 3 of 4 sets, cell 000. Refuted if above or equal on at least 3.
  • H272 (plating depth alone suffices on LG M50): F(S<sub>1</sub>)'s f* ≤ F(S<sub>C</sub>)'s on both Chen2020 and OKane2022, cell 111. Refuted if above on both.
  • Already seen: e<sub>10</sub>, e<sub>50</sub> per design (7b), m̂<sub>C</sub> and O1 per design and their correlations with m (7c), 7c's post hoc tail quantiles under its correction. Not seen: any score's ranking against e<sub>10</sub> − e<sub>50</sub>, any triage policy, any f*.
  • Risks named now: 24 to 28 designs per set, so q75 is the 7th-largest error or so and moves by whole designs; a design whose drift is large but whose 50-cycle line is no better gains nothing from extension; S<sub>C</sub> predicts the drift of the law under measured inputs (cell 111) better than the real forecast's whole error; the target (1.25 times all-50) is one choice, and f* on a 0.05 grid is coarse.

2026-11-19 · Milestone 7c outcome: ten cycles do tell which LG M50 designs will drift. With every input measured, each design's drift multiplier m tracks where the plating sits at cycle 2 (Spearman ρ = 0.80 on Chen2020 and OKane2022, Holm-adjusted permutation p = 0.0003; plating nearer the separator, faster rate) and the bend of lithium loss itself (ρ = −0.73, −0.72). A correction built on it does not lower the set-median floor (1.8% to 2.3%, 1.9% to 2.1%), because the typical design drifts by 4%, about the correction's own error, but post hoc it halves the upper quartile (8.0% to 3.5%, 7.3% to 3.0%). On the real forecast it beats the line on all four sets. H265 and H268 supported, H266 refuted, H267 inconclusive

  • Analysis: stdlib, 15 s (rows, 4 cores), tests run before the report, report run once; run.py unchanged after the plan apart from the post hoc posthoc subcommand added after the report. Reproduces 7b: the line's e at k = 10 equals 7b's on all 104 designs and cells (to 12 places, tested); the design's own m reproduces cycle 99 (e<sub>own m</sub> 0.000 at every set median, both cells).
  • H265 supported: O1 (cycle-2 plating depth) ρ = 0.796 (Chen2020) and 0.797 (OKane2022), Holm p 0.0003 on both; O3 −0.726 and −0.715 (Holm p 0.0006); O2 (the depth's change to cycle 10) −0.01 and −0.08. On Ai2020 ρ 0.37, −0.27, −0.34 (Holm p 0.24); NCA_Kim2011 −0.08, −0.18, −0.31 (none significant).
  • H266 refuted (C/L 1.30 and 1.07): set median e<sub>111</sub> L, M, C: Chen2020 0.018, 0.021, 0.023; OKane2022 0.019, 0.022, 0.021. C beats L on 14 and 16 of 28 designs. H267 inconclusive (C below M on OKane2022 only).
  • H268 supported (4 of 4): e<sub>000</sub> L to C 0.025 to 0.023 (Ai2020), 0.056 to 0.055, 0.067 to 0.046, 0.040 to 0.014 (NCA_Kim2011, 22 of 24 designs). For cell 000 every fold picks O2 on LG M50 and O1 on the other two sets.
  • Reported: m (cell 111) set medians 1.232, 0.985, 0.994, 0.904 (IQRs 1.21 to 1.27, 0.95 to 1.02, 0.94 to 1.03, 0.87 to 0.98). On Ai2020 the constant drift M is the best ten-cycle forecast found so far for cell 111 (0.007, against 7b's borrowed bend 0.048 and C's 0.018): its drift is shared, as 7b found. Per pool, C beats L on LG M50 in the two fresh pools (0.029 and 0.026 against 0.033 and 0.028 for 5zy; 0.026 and 0.019 against 0.032 and 0.034 for 5zz) and ties in 5zk.
  • Post hoc, descriptive (after the report, not hypothesised; posthoc.txt): e<sub>111</sub> quantiles L to C, Chen2020 q75 0.080 to 0.035, q90 0.101 to 0.065; OKane2022 q75 0.073 to 0.030, q90 0.090 to 0.053; the max is unchanged (0.117 to 0.113). m's spread is heavy-tailed (sd 0.12 against an IQR of ±0.04): C cuts its leave-one-out RMSE from 0.130 to 0.094 and 0.116 to 0.084 but not its median absolute error (0.043, 0.043; 0.050, 0.037). O1's correlation holds inside each pool (ρ 0.56, 0.86, 1.00 on Chen2020; 0.52, 0.90, 1.00 on OKane2022, n = 8 to 12), so it is not a pool artefact.
  • Reading: 7b's per-design drift on LG M50 is not noise. Where the plating sits at cycle 2 tells, before cycle 11, which designs' law rate will speed up or slow down over the next 90 cycles, and by roughly how much. Most designs drift too little (about 4%) for any ten-cycle correction to beat the line, which is why the median floor stays near 2%; a quarter drift by 10 to 25%, and those are the ones the correction catches, halving the upper-quartile error. For a design search that is the useful half: the risk of a badly wrong forecast is concentrated in designs whose cycle-2 plating sits far from the set's typical depth, and those can be flagged or simulated longer. On Ai2020 the drift is shared (a constant m does best), on NCA_Kim2011 it is small and unexplained. Next: the paper's results section from 5zk to 7c (the error budget, the floor and this tail correction as its tables); then a decision rule that sends only the flagged designs to a longer simulation, scored on DFN calls saved at a tail-error target.
  • Caveats: 24 to 28 designs per set and three observables; C chooses its observable inside each fold; the quantile result is post hoc; O1 is a model internal (node plating) a real cell exposes only through a diagnosis; one law form and one κ (25.3); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/drift7c/results.txt, summary.json, rows.json, posthoc.txt, drift7c.svg; tests tests/test_drift7c.py.

2026-11-19 · Milestone 7c (the per-design drift): does a ten-cycle observable predict how far each design's law rate drifts by cycle 99, and does a correction built on it close the LG M50 floor that 7b found a longer window and a borrowed bend cannot? (plan, written and committed before any observable below was correlated with any drift on these designs; H265 to H268 are this entry's)

  • Question: 7b found that on LG M50, with every input measured (cell 111), R(L) grows at a constant rate per cycle at the set median, but each design's rate drifts a few per cent either way over 99 cycles, and that drift, not a bend, is the 1.8 to 1.9% ten-cycle floor. 7b's next step: whether that per-design drift tracks something visible in ten cycles (where the plating sits, how it moves, how lithium loss itself bends).
  • Target, per design and cell: the drift multiplier m, defined by R(99) = a + 10 s + 89 s m, with (a, s) the ten-cycle line through R(L<sub>n</sub>), n = 2..10, and R(99) = R(L<sub>DFN</sub>(99)) on the cell's table (m = 1 is 7a's/7b's line L; the forecast at m is inverted as L is). Ten-cycle observables, fixed now: O1, the plating-weighted depth (centroid, 1 = separator) of cycle 2's node plating (5zk's centroid); O2, its change from cycle 2 to cycle 10; O3, the bend of lithium loss itself, ln((L<sub>10</sub> − L<sub>6</sub>)/(L<sub>6</sub> − L<sub>2</sub>)).
  • Method (experiments/drift7c/run.py, rows, report; stdlib, no new simulation): 7b's tables imported unchanged (cells 000 and 111), all 104 ok x-resolved designs (5zk 40, 5zy 32, 5zz 32), κ = 25.3, e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|. Spearman ρ of m (cell 111) with O1 to O3 within each set; two-sided permutation p (10,000 shuffles, random.Random(73)), Holm over the three observables per set. Corrections at ten cycles, leave one design out within the set: C, m̂ from a least-squares line of m on the one observable with the largest |ρ| on the other designs (chosen inside each fold); M, m̂ = the other designs' median m (a constant drift, the control: what a shared bend gives). Cell 000 gets the same with its own m.
  • H265 (the drift is predictable from ten cycles): on both LG M50 sets (Chen2020, OKane2022) some observable has |ρ| ≥ 0.5 with Holm-adjusted p < 0.05. Refuted if no observable reaches |ρ| ≥ 0.3 on either set.
  • H266 (a correction closes the floor): C's set median e<sub>111</sub> ≤ 0.75 times L's on both LG M50 sets. Refuted if C's is above L's on both.
  • H267 (beyond a shared drift): C's set median e<sub>111</sub> below M's on both LG M50 sets. Refuted if above on both.
  • H268 (it carries to the real ten-cycle forecast): C's set median e<sub>000</sub> below L's on at least 3 of 4 sets. Refuted if on 1 or none.
  • Already seen: 7b's late/early slope ratios (set medians and IQRs, cell 111 and 000), its finding that the drift's sign varies by design, and 5zk's centroids on its 40 designs. Not seen: m itself, O2, O3, or any correlation of any observable with any drift.
  • Risks named now: 24 to 28 designs per set, so |ρ| = 0.5 is near the detection limit; choosing the observable inside each fold costs power; O1 to O3 are model internals (node plating, lithium loss) a real cell exposes only through a diagnosis; m is a ratio to the ten-cycle slope and inherits that slope's noise.

2026-11-19 · Milestone 7b outcome: on LG M50 the law floor is not a bend and a longer window does not remove it. With every input measured, the set-median cycle-99 error moves from 1.8% to 1.6% (Chen2020) and 1.9% to 1.4% (OKane2022) as the law's line window grows from 10 to 50 cycles, while the real ten-cycle forecast falls from 5.6% to 2.7% and 6.7% to 2.1%: 5zm's longer-window gain on LG M50 comes from the inputs, not the law. The measured R(L) is a straight line in cycle number at the set median (late slope 0.99 times the ten-cycle slope) but scatters ±5 to 10% design by design, so a bend borrowed from other designs makes it worse (T beats L on 15 of 28 and 5 of 28). Ai2020 is the exception: its R bends upward on every design (late slope 1.24 to 1.34 times), and the borrowed bend cuts its floor from 8.3% to 4.8% (23 of 24 designs). H261 supported, H263 inconclusive, H260, H262 and H264 refuted

  • Analysis: stdlib, 15 s (rows, 4 cores), tests run before the report, report run once; run.py unchanged after the plan apart from the post hoc posthoc subcommand added after the report. Reproduces 7a: the line at k = 10 equals 5zu's and 7a's cells 000 and 111 on all 104 designs (to 1e−15, tested).
  • H260 refuted (1 of 4): set median e<sub>111</sub> at k = 10 and 50: Ai2020 0.083 and 0.020, Chen2020 0.018 and 0.016, OKane2022 0.019 and 0.014, NCA_Kim2011 0.011 and 0.007. On LG M50 the floor is flat to k = 40 (0.018 to 0.024, 0.017 to 0.021).
  • H261 supported (4 of 4): the free quadratic through cycles 2..10 is worse than the line everywhere (e<sub>111</sub> 0.129, 0.082, 0.100, ∞ on NCA_Kim2011, where its ten-cycle γ of about −0.015 per cycle puts the parabola's peak near cycle 33, so 14 of 24 forecasts cannot be inverted at cycle 99); the ten-cycle γ's set median is 9 to 100 times the 99-cycle one, with the opposite sign on NCA_Kim2011.
  • H262 refuted (1 of 4): T's e<sub>111</sub> 0.048, 0.021, 0.026, 0.011 against L's 0.083, 0.018, 0.019, 0.011. H263 inconclusive (0.021, 0.026: neither ≤ 0.015 nor both > 0.03). H264 refuted (1 of 4): T's e<sub>000</sub> 0.027, 0.079, 0.079, 0.025 against NS 0.025, 0.056, 0.067, 0.040 (NCA_Kim2011 the one win, 23 of 24 designs).
  • Reported: O, the design's own 99-cycle γ with the ten-cycle line's a and s, reaches only 0.058, 0.019, 0.017, 0.013 for e<sub>111</sub>: even a known quadratic bend does not remove the LG M50 floor, because the ten-cycle slope itself is off. γ set medians (cell 111, per cycle): 0.00088, −0.00015, −0.00007, 0.00012, with IQRs spanning zero on every set except Ai2020. e<sub>000</sub> falls with the window on every set (k = 50: 0.010, 0.027, 0.021, 0.014). Per pool, 5zk's 40 have the lowest LG M50 floor at every window, as 7a found at k = 10.
  • Post hoc, descriptive (after the report, not hypothesised; posthoc.txt): a line through all of cycles 2..99 leaves e<sub>111</sub> 0.003 to 0.005, so R(L) with measured inputs is nearly linear in cycle number over the whole run; a ten-cycle line through cycles 11..20 instead of 2..10 does no better (0.019, 0.019 on LG M50), so the first cycles are not a transient to skip. Slope of R over cycles 51..99 against 2..10, cell 111: Ai2020 1.27 (IQR 1.24 to 1.34), Chen2020 0.99 (0.90 to 1.03), OKane2022 0.99 (0.89 to 1.05), NCA_Kim2011 0.94 (0.86 to 1.06). For the real forecast (cell 000) the late slope departs further and in both directions (NCA_Kim2011 0.69, OKane2022 1.08).
  • Reading: the law is right on LG M50 in the sense that matters: with true inputs R(L) grows at a constant rate per cycle to within a few per cent over 99 cycles. What a ten-cycle line cannot know is each design's own few-per-cent drift in that rate, and the sign of the drift varies by design, so neither a set bend nor a longer line removes it until the window covers most of the run. That puts the ten-cycle forecast's irreducible error on LG M50 at about 2 to 3% (set medians 1.8 and 1.9% over all 104 designs, 2.8 to 3.4% on the fresh pools, against the 0.5% a line through all 99 cycles leaves), and the fresh pools show it is not a window problem: their floor at k = 50 is still 1.8 to 3.7%. The large window gains of 5zm on the real forecast are input gains: a longer line averages out the node lever's and the drift's errors (cell 000's slopes drift by 10 to 30%). Ai2020 has a real, shared bend (its R accelerates by a quarter over the run on every design), which is why measured inputs looked worse there in 5zu and 7a: a ten-cycle line under-reads its acceleration, and a borrowed bend recovers about half of it. For a design search: fit the law's line through 30 to 50 cycles, as before, and expect it to fix the inputs rather than the law; on Ai2020-like cells, add a bend borrowed from a few fully simulated designs. Next: the paper's results section from 5zk to 7b (the error budget and this floor as its two tables); then whether the per-design rate drift on LG M50 tracks a ten-cycle observable (SEI share of the loss, the separator-node plating fraction).
  • Caveats: one law form (line or quadratic in n) and one κ (25.3); the quadratic's γ is a crude bend model; T borrows within the set from pools of 24 to 28; inputs are model internals with cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/lawfloor/results.txt, summary.json, rows.json, posthoc.txt, lawfloor.svg; tests tests/test_lawfloor.py.

2026-11-19 · Milestone 7b (the law floor): how does the all-measured forecast error e<sub>111</sub> fall as the law's line window grows from 10 to 50 cycles, and does a curved term, its bend borrowed from the set's other designs, close it at ten cycles? (plan, written and committed before any window other than 10, 30 and 50 cycles or any curved term was computed on these designs; H260 to H264 are this entry's)

  • Question: 7a found that with every input measured (cell 111) the ten-cycle forecast still misses cycle-99 lithium loss by 3.2 to 3.4% on held-out LG M50 designs, more than half of the forecast's error there: the law's own term, a straight line in R(L) = ∫ exp(κ du) Q<sub>0</sub>/Q dl against cycle number through cycles 2..10, extrapolated to cycle 99. 7a's next step: the law floor itself on all 104 x-resolved designs, how e<sub>111</sub> falls as the window grows, and whether a curved term (5zp's bend) closes it at ten cycles.
  • Method, fixed now (experiments/lawfloor/run.py, rows, report; stdlib, no new simulation): 5zu's cell tables (experiments/budget/run.py, _row's construction, cells 000 and 111) on every ok design of depth (5zk, 40), freshnode (5zy, 32) and rangeline (5zz, 32); κ = 25.3; e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|. (a) Window: the line through cycles 2..k, k ∈ {10, 15, 20, 30, 40, 50}. (b) Curved term: R(n) = a + s (n + γ n<sup>2</sup>) through cycles 2..10 with γ fixed, a and s by least squares, read at cycle 99 and inverted as the line is. Variants: L (line, 7a's), Q (free quadratic, γ fitted on cycles 2..10 alone), T (transferred: γ = median over the same set's other designs, leave one design out, of each design's c/b from a quadratic a + b n + c n<sup>2</sup> fitted to its own cell table's R(L<sub>n</sub>) over cycles 2..99), O (oracle: the design's own γ from cycles 2..99, a ceiling, not a forecast). Each cell uses its own tables' γ (T for cell 000 borrows cell-000 bends). A forecast that cannot be inverted (R beyond the table) counts as e = ∞ in medians. Primary: set medians over all 104 designs (24, 28, 28, 24); reported per pool too.
  • Already seen: e<sub>111</sub> at k = 10 on all 104 (7a: set medians 0.083, 0.018, 0.019, 0.011 for Ai2020, Chen2020, OKane2022, NCA_Kim2011); 5zm's and 5zr's 30- and 50-cycle errors for other cells on 5zk's 40 (e.g. 5zr's e<sub>A50</sub> 0.032, 0.020, 0.017, 0.011), which suggest longer windows help; 5zp's statement that the law bends even with the true rise. Not seen: e<sub>111</sub> at any k > 10, any γ, any curved forecast.
  • H260 (a longer window removes the floor): set median e<sub>111</sub> at k = 50 ≤ half its k = 10 value on at least 3 of 4 sets. Refuted if on 1 or none.
  • H261 (the bend is not identifiable from ten cycles): Q's set median e<sub>111</sub> above L's on at least 3 of 4 sets. Refuted if on 1 or none.
  • H262 (a borrowed bend closes part of the floor): T's set median e<sub>111</sub> below L's on at least 3 of 4 sets. Refuted if on 1 or none.
  • H263 (it closes the LG M50 floor): T's set median e<sub>111</sub> ≤ 0.015 on both Chen2020 and OKane2022. Refuted if above 0.03 on both.
  • H264 (it carries to the real ten-cycle forecast): T's set median e<sub>000</sub> below L's (NS) on at least 3 of 4 sets. Refuted if on 1 or none.
  • Reported, not hypothesised: the per-set γ spread (median, IQR), O's ceiling, e<sub>000</sub> against k, and T's wins over L design by design.
  • Risks named now: a quadratic in n extrapolated 89 cycles past a ten-cycle fit amplifies any error in γ; γ may differ by design within a set as 5zw's node gains did; on Ai2020 cell 111 is already worse than cell 000, so a closer law may not help e<sub>000</sub> there.

2026-11-19 · Milestone 7a outcome: on the 64 held-out designs every direction of 5zu's error budget replicates, but its sizes do not. The node lever's OCP rise is still the largest input on OKane2022 and NCA_Kim2011, the drift on Chen2020, the capacity factor is spent everywhere, and on Ai2020 measuring the inputs still makes the forecast worse (2.9% to 8.3%). But with every input measured, the forecast still misses cycle-99 lithium loss by 3.4% on OKane2022 and 3.2% on Chen2020, against 1.5% and 1.4% on 5zk's 40: out of sample, more than half of the ten-cycle error on LG M50 (set median shares 0.57 and 0.62) is the law's own term, not any input. That answers 5zz: the law's ten-cycle line limits the forecast on the sets where the lever does not. H256 to H259 supported

  • Analysis: stdlib, 8 s (rows, 4 cores), tests run before the report, report run once; run.py unchanged after the plan apart from the post hoc rounded subcommand added after the report. Reproduces 5zy and 5zz: cell 000 equals their NS and cell 100 their C on all 64 designs (to 12 places), cell 111 equals 5zp's PQ built its way (to 6 places), each design's Shapley values sum to its gap, and no fresh design is one of 5zu's 40 (tested).
  • H256 supported (rank 1): on OKane2022 set median φ<sub>M</sub> 0.007, φ<sub>D</sub> 0.004, φ<sub>q</sub> 0.001 (gap 0.023, in sample 0.033, 0.011, −0.001, gap 0.056). M has the largest φ on 9 of 16 designs.
  • H257 supported (4 of 4 at most 0.01): set median φ<sub>q</sub> −0.004, 0.001, 0.001, −0.002.
  • H258 supported: on Ai2020 set median gap −0.062 (e<sub>000</sub> 0.029, e<sub>111</sub> 0.083); φ<sub>M</sub> negative on 13 of 16 designs, φ<sub>D</sub> on 11.
  • H259 supported (rank 1): on Chen2020 φ<sub>D</sub> 0.015, φ<sub>M</sub> 0.003, φ<sub>q</sub> 0.001 (gap 0.032); D has the largest φ on 7 of 16 designs. 5zu's tie (0.020 against 0.021) breaks toward the drift out of sample.
  • Reported: held-out set medians e<sub>000</sub>, e<sub>111</sub>, floor share e<sub>111</sub>/e<sub>000</sub>: Ai2020 0.029, 0.083, 4.99; Chen2020 0.057, 0.032, 0.62; OKane2022 0.068, 0.034, 0.57; NCA_Kim2011 0.042, 0.011, 0.21 (in sample: 0.023, 0.080, 3.92; 0.054, 0.014, 0.11; 0.067, 0.015, 0.19; 0.030, 0.011, 0.20). Both fresh pools agree on the LG M50 floor (e<sub>111</sub> 0.033 and 0.032 on Chen2020, 0.028 and 0.034 on OKane2022). On NCA_Kim2011 the lever is the error in every pool (φ<sub>M</sub> 0.038, largest on 14 of 16; e<sub>100</sub> 0.006). Paper table, all 104 designs (24, 28, 28, 24): e<sub>000</sub> 0.025, 0.056, 0.067, 0.040; e<sub>111</sub> 0.083, 0.018, 0.019, 0.011; φ<sub>M</sub> −0.017, 0.009, 0.019, 0.035; φ<sub>D</sub> −0.025, 0.016, 0.008, −0.000; φ<sub>q</sub> −0.004, 0.000, 0.000, 0.001 (experiments/heldbudget/results.txt).
  • Post hoc, descriptive (after the report, not hypothesised): (1) 5zk's depth bench, which 5zu read, was committed rounded to 7 significant digits; rounding the fresh benches the same way leaves every e<sub>111</sub> unchanged to 4 places (it moves Chen2020's e<sub>000</sub> 0.057 to 0.061, as 5zy found), so rounding does not explain the lower in-sample floor (rounded.txt). (2) Per-design e<sub>111</sub> on the two LG M50 sets, 5zk's 24 against the fresh 32: Mann–Whitney two-sided p = 0.028 (normal approximation), per set p = 0.08 (Chen2020) and 0.16 (OKane2022); Ai2020 0.95, NCA_Kim2011 0.58. So 5zk's draw had a lower law floor than either fresh pool, by more than chance would usually give on LG M50, and nothing in how it was drawn (random.Random(18)) selects for that.
  • Reading: the budget's ranking of inputs is a property of the cell, and it survives designs that never informed it: lever on OKane2022 and NCA_Kim2011, drift on Chen2020, nothing from the capacity factor, cancellation on Ai2020. Its sizes were flattering. On fresh LG M50 designs the measurable inputs together close 2.3 (OKane2022) and 3.2 (Chen2020) points of a 5.7 to 6.8% error, and the rest is the law: a straight line in R against cycle number through cycles 2..10 at κ = 25.3, which 5zo found drifts by 9 to 13% over 100 cycles even with the true lever. That is why 5zv to 5zz's lever fixes stopped paying off on fresh designs (5zz: the measured-OCP ceiling beats NS on only 14 of 32): a perfect lever lands on the law floor, and on fresh designs the floor is about half the error. For a design search the advice is unchanged and now better founded: fit the law's line through 30 to 50 cycles (5zm), which shortens the extrapolation the floor comes from. For the paper: the 104-design table is the error budget, with the in-sample and held-out columns side by side. Next: the law floor itself, on all 104 designs: how e<sub>111</sub> falls as the line's window grows from 10 to 50 cycles, and whether a curved term (5zp's bend) closes it at ten cycles; then the paper's results section from 5zk to 7a.
  • Caveats: 16 held-out designs per set from the same pools, chemistry, current and Sobol space; H256 and H258 leaned on cells 000 and 100 already seen; Shapley medians need not sum to the gap's median; the floor share is a median of per-design ratios and exceeds 1 where measuring makes things worse (Ai2020); the post hoc test is two-sided, unplanned and approximate; inputs are model internals with cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/heldbudget/results.txt, summary.json, rows.json, rounded.txt, heldbudget.svg; tests tests/test_heldbudget.py.

2026-11-19 · Milestone 7a (paper draft, the error-budget table): does 5zu's error budget of the ten-cycle forecast hold on the 64 designs 5zk to 5zx never saw? (plan, written and committed before any new cell was computed on them; H256 to H259 are this entry's)

  • Question: 5zu split the gap between the best ten-cycle forecast (NS, cell 000) and the all-measured diagnosis (cell 111) into Shapley shares of the node lever's OCP rise (M), the non-OCP drift (D) and the capacity factor (q), on 5zk's 40 designs, all of which had been read by 5zk to 5zt; its caveat was "a decomposition on known designs, not a held-out test". 5zz closed the node-profile thread and asked for the paper's error budget on all x-resolved designs, to name what limits the forecast on the sets where the lever does not. 5zy and 5zz have since simulated 64 fresh designs with the same x-resolved records, so the budget can now be tested held out, and the paper's table can be printed on 104 designs. This also starts milestone 7 (PROPOSAL.md): after 52 sub-steps of milestone 5 the programme needs its tables more than another knob.
  • Method, fixed now (experiments/heldbudget/run.py, rows, report; stdlib, no new simulation): 5zu's _row imported unchanged from experiments/budget/run.py, applied to every ok design of experiments/freshnode/bench.jsonl (5zy, 32) and experiments/rangeline/bench.jsonl (5zz, 32); κ = 25.3, line through cycles 2..10, e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|. Primary: set medians over the 16 fresh designs per set. New in the report: the law floor, the per-design share e<sub>111</sub>/e<sub>000</sub> of the forecast's error left when every input is measured (what the law's ten-cycle line itself costs). Reported, not hypothesised: the same table per fresh pool, 5zu's in-sample table recomputed from its rows, and the pooled 104-design table that goes in the paper.
  • Already seen: everything 5zk to 5zz report. On the fresh designs cell 000 (NS) and cell 100 (5zv's measured-OCP ceiling C) are already known per set (5zy: NS 0.044, 0.075, 0.072, 0.033, C 0.036, 0.041, 0.015, 0.003; 5zz: NS 0.012, 0.045, 0.051, 0.053, C 0.085, 0.070, 0.046, 0.007, sets Ai2020, Chen2020, OKane2022, NCA_Kim2011), so H256 and H258 lean on directions those suggest (C below NS on OKane2022 in both pools; C above NS on Ai2020 in 5zz's pool, below it in 5zy's). Not seen on any fresh design: cells 001, 010, 011, 101, 110, 111, any Shapley value or the floor; the drift D and factor q have never been computed on them.
  • H256 (the OCP lever carries OKane2022, 5zu's H232 held out): set median φ<sub>M</sub> is the largest of the three on OKane2022. Refuted if it is the smallest.
  • H257 (the factor is spent, 5zu's H234 held out): |set median φ<sub>q</sub>| ≤ 0.01 on at least 3 of 4 sets. Refuted if above 0.02 on 3 or more.
  • H258 (on Ai2020 the inputs' errors cancel the law's, 5zu's reported negative gap held out): set median e<sub>000</sub> − e<sub>111</sub> < 0 on Ai2020. Refuted if above 0.
  • H259 (the drift carries Chen2020, 5zu's H233 tested again): set median φ<sub>D</sub> the largest of three on Chen2020. Refuted if the smallest.
  • Caveats fixed now: 16 fresh designs per set from the same pools, chemistry, current and Sobol space as 5zk's 40, so this is a held-out test across designs, not chemistries or protocols; Shapley medians need not sum to the gap's median; M<sub>w</sub> and D<sub>w</sub> are model internals with cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-19 · Milestone 5zz outcome: on a second fresh pool of 32 DFN designs the thickness line does not hold. Fitted on all 72 earlier designs and used only inside their thickness range (29 of 32 fresh designs are), it beats the uniform node lever's set median on NCA_Kim2011 only (5.3% to 3.7%) and is worse on Ai2020 (1.2% to 3.4%), Chen2020 (4.5% to 4.7%) and OKane2022 (5.1% to 6.2%); design by design it wins 14 of 29 in range. More training designs do improve the line itself (pooled beats 5zk-only on 3 of 4 sets), but not enough. On this pool even the measured-OCP ceiling beats the uniform lever on only 14 of 32 designs, so outside NCA_Kim2011 the node lever is not what limits the ten-cycle forecast. H254 supported, H252, H253 and H255 refuted

  • Bench: 32 DFN runs to cycle 100, about 6 minutes on 3 workers, all 32 ok first time, committed at full precision (6.8 MB). Tests ran before rows and report; both were run once; nothing in run.py changed after the plan commit. The figure script was written while the bench ran.
  • Pooled training: 16, 20, 20, 16 designs; Spearman(L<sub>n</sub>, h<sub>sep</sub>) −0.29, 0.40, 0.21, 0.70 (as listed in the plan). Fresh designs in range: 6, 8, 8, 7 of 8.
  • H252 refuted (1 of 4): set median e<sub>NR</sub> against e<sub>NS</sub>: 0.034 against 0.012 (Ai2020), 0.047 against 0.045 (Chen2020), 0.062 against 0.051 (OKane2022), 0.037 against 0.053 (NCA_Kim2011).
  • H253 refuted: NL beats NS on 14 of the 29 in-range designs (one-sided sign test p = 0.64).
  • H254 supported (3 of 4): set median e<sub>NL</sub> against e<sub>NL40</sub>: 0.034 against 0.026 (Ai2020, worse), 0.047 against 0.054, 0.062 against 0.065, 0.047 against 0.048.
  • H255 refuted: on OKane2022 e<sub>NR</sub> 0.062 is above e<sub>NS</sub> 0.051 (halfway mark (0.051 + 0.046)/2).
  • Reported: set medians e<sub>NT</sub> 0.023, 0.081, 0.061, 0.045; e<sub>C</sub> 0.085, 0.070, 0.046, 0.007; e<sub>Ts</sub> 0.013, 0.076, 0.058, 0.023. NL beats NS on 2, 5, 3, 4 of 8 designs; NT on 1, 2, 4, 7. Worst fresh design under NS, NL, NR: 14.7, 19.4, 14.7% (Ai2020); 13.3, 8.9, 8.9% (Chen2020); 10.3, 8.9, 8.9% (OKane2022); 8.4, 8.8, 8.8% (NCA_Kim2011): restricting to the range removes the extrapolation tail on Ai2020 and the line trims the worst design on Chen2020 and OKane2022, but the medians move the wrong way. Lever errors N, T, L40, L, Ts (mV): 6.14, 2.50, 4.55, 2.51, 2.51; 4.28, 2.37, 4.26, 4.86, 1.52; 6.33, 5.49, 5.01, 5.38, 2.01; 25.97, 17.88, 21.49, 20.78, 1.27. 5zy's fourfold lever gain on NCA_Kim2011 (19.9 to 4.9 mV) did not replicate (26.0 to 20.8).
  • Post hoc, descriptive (computed after the report from the committed rows, not hypothesised): the measured-OCP ceiling C beats NS on 14 of 32 designs here and 23 of 32 in 5zy (37 of 64); on this pool it is worse than NS at the set median on Ai2020 (8.5% against 1.2%) and Chen2020 (7.0% against 4.5%) and beats it on all 8 NCA_Kim2011 designs. Over both fresh pools NL beats NS on 33 of 64 designs (p = 0.45).
  • Reading: 5zy's set-level gains for the thickness line were mostly the luck of one draw. On a second draw from the same pools, with more training designs and the extrapolation guard 5zy asked for, the line loses to the uniform lever at the median on three of four sets and is a coin flip design by design. The reason is upstream of the profile: replacing the uniform lever with the design's own measured anode OCP rise (C) does not reliably improve the forecast either outside NCA_Kim2011, so on Ai2020, Chen2020 and OKane2022 the ten-cycle error left after 5zm is dominated by other terms (the line extrapolation of the plating exponent and the law's other inputs), and errors in the node lever partly cancel them in either direction. NCA_Kim2011 is the exception throughout 5zv to 5zz: the lever is its error (C 0.7%), and a profile helps it on both fresh pools. For a design search: do not use a borrowed node-gain profile, except possibly on cells where the measured lever dominates; fit the law's line through 30 to 50 cycles. This closes the node-profile thread (5zv to 5zz). Next: the paper's error budget on all 104 x-resolved designs (5zk's 40 and the two fresh pools), splitting the ten-cycle error into lever, exponent and law terms, to name what limits the forecast on the three sets where the lever does not.
  • Caveats: 8 fresh designs per set; the same pools, chemistry, current and Sobol space as the training designs; Ai2020's pooled Spearman is negative (named in the plan); node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/rangeline/bench.jsonl, rows.json, results.txt, summary.json, rangeline.svg; tests tests/test_rangeline.py.

2026-11-19 · Milestone 5zz: does the anode-thickness line hold on a second fresh DFN pool once it is fitted on all 72 designs simulated so far and used only inside the training thickness range? A held-out test on 32 more designs (plan, written and committed before the fresh bench ran; H252 to H255 are this entry's)

  • Question: 5zy's thickness line (L) had the lowest set-median ten-cycle error on three of four sets out of sample, but its two worst misses on OKane2022 (14 to 15%) sat at or below the thin end of the training range, where a line extrapolates, and the pre-registered monotonicity gate fired on one set only. 5zy's own next step: restrict the line to designs inside the training thickness range (fall back to the uniform node lever NS outside), pre-registered on another fresh draw. 5zy's 32 designs are now simulated, so the line can also be fitted on 72 designs (16 to 20 per set), which widens the range it covers.
  • Bench, fixed now (experiments/rangeline/run.py bench): 8 fresh designs per set, random.Random(5252) picks from the same 64-design pools (crossset Chen2020@1.5x, OKane2022@1.5x, NCA_Kim2011@0.875x, calmap Ai2020@0.45x), excluding 5z's random.Random(18) picks, 5zy's random.Random(5248) picks and any design without a committed ok source run and balance row: Chen2020 and OKane2022 j = 0, 1, 14, 16, 32, 45, 58, 60; NCA_Kim2011 and Ai2020 j = 0, 1, 13, 27, 40, 53, 57 (NCA_Kim2011) or 58 (Ai2020), 59. Each run is 5zk's depth/run.py child unchanged (DFN, SEI + irreversible plating, 100 cycles, 20 negative-electrode nodes, PyBaMM 26.10.1.1, one fresh process per run); bench.jsonl is committed at full precision (5zy's rounding finding). A design that fails is retried once with one worker, then reported and not replaced.
  • Forecasts, fixed now (rows, stdlib): training = 5zk's 40 designs (late gains h<sub>i</sub> from experiments/nodetransfer/rows.json) plus 5zy's 32 (from experiments/freshnode/rows.json), all designs of the fresh design's set; no profile reads anything of the fresh design past cycle 10 (its anode thickness is known before simulation). L = 5zx's per-node least-squares line of h<sub>i</sub> in anode thickness on the 72-design pool, clipped to [0, 3]; R (primary) = L when the fresh design's anode thickness lies inside [min, max] of its set's pooled training thicknesses, else NS; L40 = the same line on 5zk's 40 only (5zy's L); T = node-wise median of the pooled h<sub>i</sub>. Each through 5zw's _second unchanged (κ = 25.3, line through cycles 2..10 on 5zm's tables, q<sub>S</sub>, no drift); NS, C (measured-OCP ceiling) and Ts (own late gains, reads cycle 99) from 5zw's _first unchanged. e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over the fresh designs.
  • Already seen: everything 5zk to 5zy report, including 5zy's fresh-design errors and the two thin-design misses that motivate R. While writing the code, before this plan was committed, the pooled training pools were listed: 16, 20, 20, 16 designs per set (Ai2020, Chen2020, OKane2022, NCA_Kim2011), thickness ranges 67..164, 57..188, 57..188, 92..234 μm, and pooled training Spearman(L<sub>n</sub>, h<sub>sep</sub>) −0.29, 0.40, 0.21, 0.70. No fresh design of this draw has been x-resolved, and no node gain, lever or forecast has been computed on any of them.
  • H252 (the range-restricted line holds): set median e<sub>NR</sub> < e<sub>NS</sub> on at least 3 of 4 sets. Refuted if on at most 1.
  • H253 (design by design, inside the range): e<sub>NL</sub> < e<sub>NS</sub> on enough of the in-range fresh designs (all sets pooled) for a one-sided sign test p ≤ 0.05. Refuted if on at most half.
  • H254 (more training designs help the line): set median e<sub>NL</sub> < e<sub>NL40</sub> on at least 3 of 4 sets. Refuted if on at most 1.
  • H255 (OKane2022 reaches halfway): set median e<sub>NR</sub> ≤ (e<sub>NS</sub> + e<sub>C</sub>)/2 on OKane2022. Refuted if above e<sub>NS</sub>.
  • Reported, not hypothesised: NT, NL and NL40 on every set and their win counts against NS; the number of fresh designs in range; the worst fresh design per set under NS, NL and NR; lever errors of N, T, L40, L, Ts.
  • Caveats fixed now: 8 fresh designs per set; same pools, chemistry, current and Sobol space as the training designs, so this is transfer across designs, not chemistries or protocols; Ai2020's pooled Spearman is negative, so a line in thickness there has no mechanism behind it and H252 may turn on it; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zy outcome: on 32 fresh DFN designs the profiles learned on 5zk's 40 still help, but by less, and the pre-registered gate fires only where it matters least. The thickness line has the lowest set-median ten-cycle forecast error of every profile on three of four sets (OKane2022 7.2% to 5.6%, Chen2020 7.5% to 6.5%, NCA_Kim2011 3.3% to 2.5%; Ai2020 4.4% to 5.0%), yet the gate (training Spearman ≥ 0.5) fires on NCA_Kim2011 only (0.73; OKane2022 0.46), so the gated forecast leaves OKane2022 at the uniform lever. 5zw's median profile replicates on OKane2022 (7.2% to 6.2%). Design by design no profile beats the uniform lever reliably (NL 19 of 32, NK 17, NT 16). H248 and H251 supported, H249 and H250 inconclusive

  • Bench: 32 DFN runs to cycle 100, about 5 minutes on 3 workers; Ai2020 j = 30 was killed for memory (exit −9) and finished on a single-worker retry, so all 32 designs are in. Rows (49 s, 4 cores) and the report were run once after tests passed. Then, before any reading, one change was tried and undone: rounding bench.jsonl to 7 significant digits (as 5zk did) moved Chen2020's medians by up to 0.6 points (e<sub>NK</sub> 7.0 to 7.6%), because per-cycle increments are differences of cumulative totals; the bench was re-run at full precision (2 workers, 32 of 32 ok) and reproduced the first report character for character, and that full-precision file is the one committed (6.8 MB). So 5zk's rounded file is a reproducibility risk for any step that differences its cumulative totals; 5zk to 5zx's printed numbers came from the same rounded file they were run on, so they reproduce, but they carry that rounding.
  • Gate (training designs, computed after the plan): Spearman(L<sub>n</sub>, h<sub>sep</sub>) −0.45 (Ai2020), 0.42 (Chen2020), 0.46 (OKane2022), 0.73 (NCA_Kim2011). The gate fires on NCA_Kim2011 only; 5zx's figure had suggested OKane2022 too.
  • H248 supported (1 of 1 gated set): NCA_Kim2011 set median e<sub>NG</sub> = e<sub>NL</sub> 0.025 against e<sub>NS</sub> 0.033.
  • H249 inconclusive: OKane2022 e<sub>NL</sub> 0.056, below e<sub>NS</sub> 0.072 but above the halfway mark (0.072 + 0.015)/2 = 0.044.
  • H250 inconclusive: NL beats NS on 6 of the 8 gated designs (one-sided sign test p = 0.145; the plan named 12 of 16 if two sets were gated).
  • H251 supported: OKane2022 e<sub>NT</sub> 0.062 against e<sub>NS</sub> 0.072.
  • Reported: set medians e<sub>NS</sub>, e<sub>NT</sub>, e<sub>NK</sub>, e<sub>NL</sub>, e<sub>C</sub>, e<sub>Ts</sub>: Ai2020 0.044, 0.054, 0.056, 0.050, 0.036, 0.038; Chen2020 0.075, 0.075, 0.070, 0.065, 0.041, 0.046; OKane2022 0.072, 0.062, 0.067, 0.056, 0.015, 0.047; NCA_Kim2011 0.033, 0.028, 0.029, 0.025, 0.003, 0.011. Wins over NS, all 32: NT 16, NK 17, NL 19 (p = 0.19). Lever errors N, T, K, L (mV): 2.28, 0.94, 1.33, 0.67; 4.36, 3.55, 3.25, 3.72; 7.06, 2.37, 2.09, 3.05; 19.94, 17.83, 16.71, 4.92: every transferred profile reads the cycle-99 OCP rise better than the uniform lever on every set, as in 5zw. Fresh designs outside the training thickness range: 1, 4, 4, 3 of 8.
  • Reading: the profiles' lever gains hold out of sample (H240's pattern replicates on all four sets), and on NCA_Kim2011 the thickness line cuts the lever error fourfold (19.9 to 4.9 mV) and the forecast error by a quarter. But a better lever buys less forecast than it did in-sample: the fresh OKane2022 designs have a much lower measured-OCP ceiling (1.5% against 3.5% on 5zk's designs), so most of their ten-cycle error is the lever, and the profiles close a third or less of it. The errors are heavy-tailed design by design: on OKane2022 the line takes four designs from 6 to 8% to 1 to 4% and misses two by 14 to 15%, both at or below the training range's thin end (80 and 93 μm against a training minimum of 92), where a line in thickness extrapolates. The pre-registered gate was the weak part: 0.5 was a guess and OKane2022 sat just under it (0.46), so the gated forecast threw away the set's largest median gain. For a design search the advice changes little: fit the law's line through 30 to 50 cycles; on cells like NCA_Kim2011, where the separator-node gain rises clearly with anode thickness, a thickness-line profile from a few fully simulated designs shortens that to ten cycles; elsewhere it is a set-level improvement with large single-design misses, not a rule. Next: restrict the line to designs inside the training thickness range (fall back to NS outside), pre-registered on another fresh draw; and the paper's error-budget table (the 5zu budget on these 32 designs as its held-out column).
  • Caveats: 8 fresh designs per set; the same pools, chemistry, current and Sobol space as the training designs, so this is transfer across designs, not chemistries or protocols; the gate threshold was chosen, not tuned, and its training statistic was known only after the plan; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/freshnode/bench.jsonl, rows.json, results.txt, summary.json, freshnode.svg; tests tests/test_freshnode.py.

2026-11-18 · Milestone 5zy: do the node-gain profiles learned on 5zk's 40 designs carry the ten-cycle forecast to designs they never saw? A held-out test on a fresh DFN pool of 32 designs, with the thickness line pre-registered behind a monotonicity gate (plan, written and committed before the fresh bench ran and before the gate's training statistic was computed; H248 to H251 are this entry's)

  • Question: 5zw's set-median late-gain profile (T) and 5zx's per-node thickness line (L) were judged leave-one-design-out on the 40 designs that motivated them, and L was reported, not hypothesised. 5zx's own next step: pre-register the thickness line, with a monotonicity check on the training designs that falls back to the uniform node lever, on designs the programme has never x-resolved. Does it hold out of sample?
  • Bench, fixed now (experiments/freshnode/run.py bench): 8 fresh designs per set, random.Random(5248) picks from the same 64-design pools 5z drew from (crossset Chen2020@1.5x, OKane2022@1.5x, NCA_Kim2011@0.875x, calmap Ai2020@0.45x), excluding all of 5z's random.Random(18) picks and any design without a committed ok source run and balance row: Chen2020 and OKane2022 j = 5, 13, 19, 20, 22, 33, 38, 50; NCA_Kim2011 and Ai2020 j = 11, 18, 19, 20, 30, 36, 47, 55. Each run is 5zk's depth/run.py child unchanged (DFN, SEI + irreversible plating, 100 cycles, 20 negative-electrode nodes, PyBaMM 26.10.1.1, one fresh process per run). A design that fails is reported and not replaced.
  • Forecasts, fixed now (rows, stdlib): training = 5zk's 40 designs, their late gains h<sub>i</sub> read unchanged from experiments/nodetransfer/rows.json; every profile is fitted on all training designs of the fresh design's set and read nothing of the fresh design past cycle 10 (its design vector and anode thickness are known before simulation). T = node-wise median of the training h<sub>i</sub>; K = median over the 3 training designs nearest in 5zx's scaled design cube; L = 5zx's per-node least-squares line of h<sub>i</sub> in anode thickness, clipped to [0, 3]; G (primary) = L on a set whose training designs have Spearman(L<sub>n</sub>, h<sub>sep</sub>) ≥ 0.5 (the gate), else the uniform node lever N. Each through 5zw's _second unchanged (κ = 25.3, line through cycles 2..10 on 5zm's tables, q<sub>S</sub>, no drift); NS, C (measured-OCP ceiling) and Ts (own late gains, reads cycle 99) from 5zw's _first unchanged. e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over the fresh designs.
  • Already seen: everything 5zk to 5zx report on the 40 training designs, including 5zx's reading that the separator-node late gain rises with anode thickness on OKane2022 and NCA_Kim2011 and not on Ai2020 and Chen2020 (a figure, not the Spearman statistic; so the gate is expected to fire on those two sets, and the test is on the fresh designs, not the gate). The fresh designs' booked totals at their earlier pool currents were in the source pools' benches (5zb to 5zg read those pools); none was ever x-resolved, and no node gain, lever or ten-cycle forecast of this kind has been computed on any of them.
  • H248 (the gated line holds out of sample): on every set where the gate fires, set median e<sub>NG</sub> < e<sub>NS</sub>. Refuted if on none of them (untestable if the gate fires nowhere).
  • H249 (OKane2022 reaches halfway): fresh set median e<sub>NL</sub> ≤ (e<sub>NS</sub> + e<sub>C</sub>)/2 on OKane2022. Refuted if above e<sub>NS</sub>.
  • H250 (design by design, gated sets): e<sub>NL</sub> < e<sub>NS</sub> on enough gated designs for a one-sided sign test p ≤ 0.05 (12 of 16 if the gate fires on two sets). Refuted if on at most half.
  • H251 (5zw's median profile replicates on OKane2022): fresh set median e<sub>NT</sub> < e<sub>NS</sub> there. Refuted if above.
  • Reported, not hypothesised: NK and NL on every set and their win counts against NS; the training Spearman per set; lever errors of N, T, K, L, Ts; the separator-node gain error of T, K, L; fresh designs outside the training thickness range.
  • Caveats fixed now: 8 fresh designs per set is a small test; the designs come from the same pools and the same Sobol design space as the training designs, so this tests transfer across designs of one chemistry and current, not across chemistries or protocols; the gate threshold 0.5 is chosen, not tuned; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zx outcome: matching the borrowed node-gain profile to the held-out design's three nearest neighbours does not beat 5zw's set-wide median. It keeps OKane2022's gain (6.7% to 4.5%, median 4.1%) and predicts the separator node's late gain better on three sets, but leaves Chen2020 (6.5%) and NCA_Kim2011 (4.1%) as bad as the median, beating it on one set of four. A per-node line in anode thickness (reported, not hypothesised) does better on the two sets where the late gain rises with thickness: 2.7% on OKane2022 (below the 3.5% measured-OCP ceiling) and 1.5% on NCA_Kim2011 (NS 3.0%), but 3.7% on Ai2020 (NS 2.3%) and 6.7% on Chen2020. H246 supported, H244 and H245 refuted, H247 inconclusive

  • Analysis: stdlib, about 40 s on 4 cores (rows), tests run before the report, report run once. After the plan only the test file's float comparison in test_scale_maps_bounds_to_unit_cube changed (exact equality to almostEqual); run.py did not. Reproduces 5zw: NT recomputed with 5zw's profiles through the same _second equals 5zw's on all 40 designs (to 12 places, tested); every K and L gain lies on [0, 3].
  • H244 refuted (1 of 4): set median e<sub>NK</sub> against e<sub>NT</sub> is 0.023 against 0.022 (Ai2020), 0.065 against 0.065 (Chen2020), 0.045 against 0.041 (OKane2022), 0.041 against 0.042 (NCA_Kim2011). NK beats NT on 5/8, 8/12, 8/12, 4/8 designs.
  • H245 refuted (0 of 2): e<sub>NK</sub> 0.065 against e<sub>NS</sub> 0.054 on Chen2020, 0.041 against 0.030 on NCA_Kim2011.
  • H246 supported: on OKane2022 set median e<sub>NK</sub> 0.045, below the halfway mark 0.051.
  • H247 inconclusive: NK beats NS on 22 of 40 designs (1/8, 8/12, 8/12, 5/8).
  • Reported: set median lever error N, T, K, L: 3.52, 1.73, 2.03, 2.09 mV (Ai2020); 5.08, 3.70, 3.47, 4.22 (Chen2020); 5.89, 5.31, 3.40, 4.28 (OKane2022); 23.24, 19.41, 17.97, 10.67 (NCA_Kim2011). Set median e<sub>NL</sub> 0.037, 0.067, 0.027, 0.015 against e<sub>C</sub> 0.035, 0.039, 0.035, 0.010; NL beats NS on 1/8, 8/12, 9/12, 6/8 designs (24 of 40). Set-median |t<sub>20</sub> − h<sub>20</sub>| at the separator node, T, K, L: 0.25, 0.23, 0.71 (Ai2020); 0.34, 0.18, 0.29 (Chen2020); 0.32, 0.18, 0.30 (OKane2022); 0.18, 0.18, 0.11 (NCA_Kim2011). Median distance to the third neighbour in the unit design cube: 0.75, 0.61, 0.61, 0.74.
  • Reading: the neighbours are not near (third-neighbour distance 0.6 to 0.75 of the cube's side), the risk the plan named, and although they predict the separator node's gain about twice as well as the median on Chen2020 and OKane2022, that does not reach the forecast: the set medians of NK and NT agree to half a point everywhere and NK's wins over NS (8 of 12 on Chen2020) sit beside a worse median, so the misses are a few large ones (Chen2020 designs at 148 to 172 μm are 9 to 17% off under every lever). The thickness line is the more useful lead: on OKane2022 and NCA_Kim2011 the separator node's late gain rises with anode thickness (figure), and a two-parameter line per node fitted on 7 to 11 other designs takes the forecast to or below the measured-OCP ceiling. It fails where the gain is not monotone in thickness (Ai2020's 2.55 at 102 μm and 0.23 to 0.26 above 139 μm; Chen2020's 0.00 at 169 μm), so the line is a set-specific find made after the plan, not yet a fix. For a design search the advice is unchanged: fit the law's line through 30 to 50 cycles; on OKane2022-like cells, a node-gain profile from a few fully simulated designs (median or thickness line) shortens that to ten cycles. Next: pre-register the thickness line, with a monotonicity check on the training designs that falls back to NS, on a fresh DFN pool (needs PyBaMM, absent from this container); and the error budget as the paper's table.
  • Caveats: leave-one-design-out on one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zw; NL was reported, not hypothesised, and its success is judged after seeing it; k = 3 and the thickness feature were fixed before looking, not tuned; several separator-node late gains sit on the grid ends (0.00 on two OKane2022 and one Chen2020 design, 3.00 on three NCA_Kim2011 designs), so those gains are weakly determined; the designs are not a random sample; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/nodematch/results.txt, summary.json, rows.json, nodematch.svg; tests tests/test_nodematch.py.

2026-11-18 · Milestone 5zx: does a node-gain profile matched to the held-out design carry the cycle-99 forecast where 5zw's set-wide median did not? A leave-one-design-out test of a nearest-neighbour profile and of a per-node line in anode thickness (plan, written and committed before any matched profile, lever or forecast below was computed; H244 to H247 are this entry's)

  • Question: 5zw's set-median late-gain profile (T) took OKane2022's ten-cycle forecast from 6.7% to 4.1% but made Chen2020 (5.4 to 6.5%) and NCA_Kim2011 (3.0 to 4.2%) worse, where the separator node's late gain spreads widely across designs (IQR 0.91..1.34, 2.46..3.00). With each design's own late gains a constant-gain lever reaches the measured-OCP ceiling on every set (Ts), so the open problem is predicting the profile from the design. A design search knows each design's parameters before simulating it; does conditioning the borrowed profile on them recover the design-specific part?
  • Method, fixed now (experiments/nodematch/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs; 5zw's _ctx, _second, late gains h<sub>i</sub> and its NS, NT, C imported or read from experiments/nodetransfer/rows.json unchanged). Design vector x = (positive thickness, positive porosity, negative porosity, relative N/P ratio) from bench.jsonl, scaled to the unit cube by energy_cell.cell.BOUNDS (50..150 μm, 0.20..0.40, 0.20..0.40, 0.90..1.30). K (primary): t<sub>i</sub> = node-wise median of h<sub>i</sub> over the k = 3 other designs of the same set nearest in scaled Euclidean distance (ties by design index). L: t<sub>i</sub> = a per-node least-squares line of h<sub>i</sub> against anode thickness L<sub>n</sub> (from bench.jsonl) over the other designs of the set, evaluated at the held-out L<sub>n</sub> and clipped to 5zv's gain grid [0, 3]. Forecasts NK = (K, q<sub>S</sub>) and NL = (L, q<sub>S</sub>) at κ = 25.3, line through cycles 2..10 on 5zm's tables, no drift, through 5zw's _second unchanged; NS, NT and the ceiling C as 5zw (reproduced from its rows). Lever error and e as 5zw; set medians over 8, 12, 12, 8 designs.
  • Already seen: everything 5zk to 5zw report on these designs, including every design's late gains h<sub>i</sub>, T, NT, NS, C and Ts, and the separator-node spread. Not seen: any design's distance to another, any nearest-neighbour or thickness-line profile, NK or NL on any design, or how h<sub>i</sub> varies with any design parameter. Risk named now: 8 to 12 designs in four dimensions are sparse, so the 3 nearest neighbours of a design are not near and K may be no better than a noisier median; L spends two parameters per node on 7 to 11 points and can extrapolate at the thickness extremes.
  • H244 (conditioning beats the set median): set median e<sub>NK</sub> < e<sub>NT</sub> on at least 3 of 4 sets. Refuted if on at most 1.
  • H245 (repairs the sets T hurt): set median e<sub>NK</sub> ≤ e<sub>NS</sub> on both Chen2020 and NCA_Kim2011. Refuted if e<sub>NK</sub> > e<sub>NS</sub> on both.
  • H246 (keeps OKane2022): set median e<sub>NK</sub> on OKane2022 at most (e<sub>NS</sub> + e<sub>C</sub>)/2 (5zw's halfway mark, 0.051). Refuted if above e<sub>NS</sub>.
  • H247 (design by design): e<sub>NK</sub> < e<sub>NS</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • Reported, not hypothesised: NL's lever and forecast errors and counts; set medians of the lever errors of K and L; the set-median absolute error of the separator node's predicted gain |t<sub>20</sub> − h<sub>20</sub>| for T, K and L; the median distance to the third neighbour; counts NK<NT and NL<NS per set.
  • Caveats fixed now: leave-one-design-out on one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zw, so held out from the profile's fit but not from the programme's earlier choices (5zw's failure motivated this test); k = 3 and the thickness feature are chosen before looking, not tuned; the designs are not a random sample; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zw outcome: a node-gain profile carried from the other designs of a set takes OKane2022's cycle-99 lithium-loss forecast from 6.7% to 4.1% (set median; the measured-OCP ceiling is 3.5%), and reads the OCP rise better than the uniform lever on all four sets, but it makes Chen2020 (5.4 to 6.5%) and NCA_Kim2011 (3.0 to 4.2%) worse and beats the uniform lever on 23 of 40 designs. Relaxing the design's own ten-cycle gains at a rate chosen on the other designs helps OKane2022 too (4.7%, 9 of 12) but is no better than both NS and NG on three sets. H240 and H241 supported, H242 refuted, H243 inconclusive

  • Analysis: stdlib, 34 s on 4 cores (rows), tests run before the report, report run once, nothing in experiments/nodetransfer/run.py changed after the plan apart from the test file's float comparison. Δs was fixed in the plan to the line-extrapolated L̂<sub>99</sub> before any code ran. Reproduces 5zv: NS, NG and C equal 5zv's on all 40 designs (to 12 places), the ten-cycle gains are identical, and R at ρ = ∞ equals G (tested).
  • H240 supported (4 of 4): set median lever error, T against N, 1.73 against 3.52 mV (Ai2020), 3.70 against 5.08 (Chen2020), 5.31 against 5.89 (OKane2022), 19.41 against 23.24 (NCA_Kim2011).
  • H241 supported: on OKane2022 set median e<sub>NT</sub> 0.041, below the halfway mark (0.067 + 0.035)/2 = 0.051; NT beats NS on 7 of 12 designs there.
  • H242 refuted (1 of 4): set median e<sub>NR</sub> 0.025, 0.040, 0.047, 0.057 against min(e<sub>NS</sub>, e<sub>NG</sub>) 0.023, 0.039, 0.067, 0.023; only OKane2022 passes.
  • H243 inconclusive: NT beats NS on 23 of 40 designs (2/8, 8/12, 7/12, 6/8).
  • Reported: set median e<sub>NT</sub> 0.022, 0.065, 0.041, 0.042 against e<sub>NS</sub> 0.023, 0.054, 0.067, 0.030. The in-sample constant-gain lever with the design's own late gains (Ts, reads cycle 99) reaches 0.021, 0.039, 0.030, 0.021, at or below the measured-OCP ceiling C on every set, and its lever error is 1.1 to 1.9 mV: a constant per-node gain is enough if it is the right one. Set-median late gains, collector to separator: Ai2020 0.85 ... 1.07; Chen2020 0.61 ... 1.17; OKane2022 0.52, 0.58, 0.56, 0.78, 0.96, 0.78, 0.72, 1.01; NCA_Kim2011 1.07 ... 2.83. Separator-node IQR across designs: 1.04..1.10, 0.91..1.34, 0.79..1.23, 2.46..3.00. The LOO ρ: ∞ on all 8 Ai2020 designs, 10 on 11 of 12 Chen2020, 0.5 or 1 on OKane2022, and 0.5 on 3 and 5 on 5 NCA_Kim2011 designs (unstable).
  • Reading: the late gains (0.5 to 1.0 on OKane2022) sit well above 5zv's ten-cycle gains (0.1 to 0.8): the node lag shrinks with lithium lost, as 5zv's failure implied, and once the per-node gains are right a constant gain is enough (Ts). Two designs of the same chemistry share enough of that late profile on OKane2022 that a median carried across designs recovers 2.6 of the 3.2 points between NS and the measured-OCP ceiling. It does not carry on Chen2020 and NCA_Kim2011, where the separator node's late gain spreads widely across designs (IQR 0.91 to 1.34; 2.46 to 3.00, at the grid end), so the median erases the design-specific part, the risk the plan named. The per-design win counts (23 of 40) say the transfer is a set-level fix on OKane2022, not a rule. For a design search the advice is: with a few fully simulated designs of the same chemistry, carry their node-gain profile into the ten-cycle forecast on OKane2022-like cells; otherwise fit the law's line through 30 to 50 cycles. Next: condition the transferred profile on the design (nearest-neighbour or a regression of h<sub>i</sub> on thickness, porosity and rate), and a held-out pool of new DFN designs for T and G4 (needs PyBaMM, absent from this container).
  • Caveats: leave-one-design-out on one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zv, so held out from the profile's fit but not from the programme's earlier choices; the designs are not a random sample; gains weakly determined on plateau nodes and NCA_Kim2011's separator gain sits on the grid end (3.00); node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/nodetransfer/results.txt, summary.json, rows.json, nodetransfer.svg; tests tests/test_nodetransfer.py.

2026-11-18 · Milestone 5zw: does a node-gain profile learned on the other designs of a set carry the cycle-99 forecast, where 5zv's own ten-cycle gains did not? A leave-one-design-out test of a transferred late gain and of a relaxing gain (plan, written and committed before any late gain, relaxation, lever or forecast below was computed; H240 to H243 are this entry's)

  • Question: 5zv's per-node gains fitted on cycles 3..10 under-read OKane2022's cycle-99 OCP rise (lever error 14.8 against N's 5.9 mV): the node lag is not a constant fraction of the uniform shift. A design search that has fully simulated a few designs of a chemistry can learn how the node lag evolves from them. Two ways to use that, both held out design by design within a set: (T) carry the other designs' late per-node gain profile; (R) let the design's own ten-cycle gains relax toward 1 with a shared rate chosen on the other designs.
  • Method, fixed now (experiments/nodetransfer/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs; 5zv's fit_gain, gain_lever and its forecast pipeline imported unchanged). Late gain h<sub>i</sub> per design and node = 5zv's fit_gain over cycles 3..99 (reads past cycle 10, so used only for other designs). T: constant gains t<sub>i</sub> = median over the other designs of the same set of h<sub>i</sub> (leave one design out); lever G with gains t<sub>i</sub>. R: path gains g<sub>i</sub>(l) = 1 + (g<sub>i</sub> − 1) exp(−max(0, s(l) − s(L<sub>10</sub>))/(ρ Δs)), g<sub>i</sub> the design's own 5zv gain, Δs = s(L̂<sub>99</sub>) − s(L<sub>10</sub>), with L̂<sub>99</sub> the lithium lost at cycle 99 extrapolated by a least-squares line through cycles 2..10 (no DFN read past cycle 10), ρ on the grid 0.05, 0.1, 0.2, 0.5, 1, 2, 5, 10, ∞ chosen per held-out design as the value minimising the median forecast error e over the other designs of its set; lever R(l) = Σ w<sub>i</sub> [U<sub>n</sub>(x<sub>i</sub>(2) + g<sub>i</sub>(l) s(l)) − U<sub>n</sub>(x<sub>i</sub>(2) + g<sub>i</sub>(0) s(0))]; ρ = ∞ is 5zv's G (tested), ρ → 0 is N past cycle 10. Forecasts NT = (T, q<sub>S</sub>) and NR = (R, q<sub>S</sub>) at κ = 25.3, line through cycles 2..10 on 5zm's tables, no drift; NS, NG and the ceiling C as in 5zv (reproduced). Lever error |du(L<sub>99</sub>) − du(L<sub>2</sub>) − M<sub>w,99</sub>| in mV; e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over 8, 12, 12, 8 designs.
  • Already seen: everything 5zk to 5zv report on these designs, including N's, G's and G4's lever errors, NS, NG, NG4 and C. Not seen: any late gain h<sub>i</sub>, any transferred profile, any relaxation or ρ, NT or NR on any design. Risk named now: within a set the designs differ in thickness, porosity and rate (5zk), so node i is a different depth and lag on each; a median profile may average away exactly the design-specific lag that matters, and 8 to 12 designs is a small training pool.
  • H240 (the transferred profile reads the OCP rise): set median T lever error below N's on at least 3 of 4 sets. Refuted if on at most 1.
  • H241 (and carries OKane2022): set median e<sub>NT</sub> at most (e<sub>NS</sub> + e<sub>C</sub>)/2 on OKane2022. Refuted if above e<sub>NS</sub>.
  • H242 (relaxation does no harm and some good): set median e<sub>NR</sub> ≤ min(e<sub>NS</sub>, e<sub>NG</sub>) on at least 3 of 4 sets. Refuted if on at most 1.
  • H243 (design by design): e<sub>NT</sub> < e<sub>NS</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • Reported, not hypothesised: set-median late gains h<sub>i</sub> by node, the spread (IQR) of h<sub>i</sub> across designs at the separator node, the ρ chosen per set (median), counts NT<NS and NR<NS per set, and T's error with the design's own h<sub>i</sub> (an in-sample ceiling for a constant-gain lever, reads cycle 99).
  • Caveats fixed now: leave-one-design-out on one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zv, so held out from the profile's fit but not from the programme's earlier choices; the designs are not a random sample of a design space; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zv outcome: a per-node gain fitted on cycles 3..10 does not carry the ten-cycle forecast. On OKane2022 the gains fall well below 1 (plating-weighted mean 0.61), the lever under-reads the cycle-99 OCP rise by 14.8 mV (N: 5.9) and the forecast is 6.9% off against NS's 6.7%; it helps Chen2020 (5.4 to 3.9%, the measured-OCP ceiling) and NCA_Kim2011 (3.0 to 2.3%) and beats NS on 22 of 40 designs. Gains on the four separator-side nodes only (G4, reported, not hypothesised) take OKane2022's set median to 4.1% but beat NS on only 6 of 12 designs there and 20 of 40 overall, and make Chen2020 worse (6.9%). H237 and H238 refuted, H236 and H239 inconclusive

  • Analysis: stdlib, 40 s (rows), tests run before the report, report run once, nothing in experiments/nodegain/run.py changed after the plan. Reproduces 5zu: NS equals cell 000 and C equals cell 100 on all 40 designs (to 12 places), and G with every gain 1 equals 5zn's N (tested).
  • H236 inconclusive (2 of 4): set median lever error at cycle 99, G against N, is 6.58 against 3.52 mV (Ai2020), 2.52 against 5.08 (Chen2020), 14.83 against 5.89 (OKane2022), 17.20 against 23.24 (NCA_Kim2011).
  • H237 refuted: on OKane2022 set median e<sub>NG</sub> 0.069 against e<sub>NS</sub> 0.067.
  • H238 refuted: the halfway mark was 0.051 (NS 0.067, ceiling C 0.035).
  • H239 inconclusive: NG beats NS on 22 of 40 designs (4/8, 7/12, 6/12, 5/8).
  • Reported: set median e of NS, NG, NG4, C is 0.023, 0.025, 0.025, 0.035 (Ai2020); 0.054, 0.039, 0.069, 0.039 (Chen2020); 0.067, 0.069, 0.041, 0.035 (OKane2022); 0.030, 0.023, 0.015, 0.010 (NCA_Kim2011). G4's lever error is 1.36, 6.25, 5.07, 11.28 mV. NG4 beats NS on 2/8, 4/12, 6/12, 8/8 designs. Set-median gains from the collector (node 1) to the separator (node 20), every third node and the last: Ai2020 0.93 ... 0.45, 0.19; Chen2020 0.67 ... 0.96, 1.00; OKane2022 0.16, 0.33, 0.13, 0.83, 0.82, 0.49, 0.17, 0.75; NCA_Kim2011 1.14 ... 0.90, 3.00. Plating-weighted mean gain 0.79, 0.96, 0.61, 1.27.
  • Reading: over cycles 3..10 the anode nodes' local OCP rises more slowly than the uniform shift predicts on three sets, most on OKane2022 (gains 0.1 to 0.8), but extrapolating that ratio to cycle 99 over-corrects: N over-reads early (5zo) and under-reads late less than G does. So the node lag is not a constant fraction of the shift, the same failure as 5zq's drift line, and the risk the plan named. On Chen2020 the gain lever reaches the measured-OCP ceiling (3.9%), which says its OCP share (5zu's φ<sub>M</sub> 2.1) is recoverable from ten cycles there. G4's set-median win on OKane2022 is a median of mixed designs (6 of 12) and found after the plan, so it is a lead, not a result; NCA_Kim2011 is the one set where G4 wins everywhere (8 of 8). For a design search the advice is unchanged: fit the law's line through 30 to 50 cycles. Next: a gain that is allowed to relax with lithium lost (two parameters per node, or one shared relaxation) tested on held-out designs, and G4 pre-registered on fresh designs before it is called a fix.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zu, so a check on known designs, not a held-out test; G4 was reported, not hypothesised; s moves by under a tenth of its cycle-99 value within cycles 3..10, so gains are weakly determined on flat plateau nodes (ties go to 1; NCA_Kim2011's separator node sits on the grid end, 3.00); node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/nodegain/results.txt, summary.json, rows.json, nodegain.svg; tests tests/test_nodegain.py.

2026-11-18 · Milestone 5zv: does a ten-cycle per-node gain on the node lever's shift forecast the plating-weighted OCP rise, and close OKane2022's OCP share of the ten-cycle error? (plan, written and committed before any gain, lever or forecast below was computed; H236 to H239 are this entry's)

  • Question: 5zu put the largest share of OKane2022's ten-cycle error (φ<sub>M</sub> 3.3 of a 5.6-point gap) in the node lever's OCP part: 5zn's lever moves every node's stoichiometry by the same uniform shift s(l), and 5zo found its over-read sits at the deepest-lithiated, separator-side nodes where the plating is. A node whose local stoichiometry moves less (or more) than the uniform shift is invisible to that lever. Cycles 2..10 already show each node's measured OCP rise, so a per-node gain on s can be calibrated there without reading past cycle 10.
  • Method, fixed now (experiments/nodegain/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs, 5zu's, 5zt's and 5zn's code imported unchanged). For each node i, gain g<sub>i</sub> = the value on the grid 0.00, 0.01, ..., 3.00 minimising Σ<sub>n=3..10</sub> [U<sub>n</sub>(x<sub>i</sub>(2) + g s(L<sub>n</sub>)) − U<sub>n</sub>(x<sub>i</sub>(2)) − (u<sub>i</sub>(n) − u<sub>i</sub>(2))]<sup>2</sup>, fitted in OCP space so the graphite plateau's flat steps cannot blow up an inverse (ties go to the gain nearest 1). Gain lever G(l) = Σ w<sub>i</sub> [U<sub>n</sub>(x<sub>i</sub>(2) + g<sub>i</sub> s(l)) − U<sub>n</sub>(x<sub>i</sub>(2) + g<sub>i</sub> s(0))], cycle-2 weights; with g<sub>i</sub> = 1 it is 5zn's N (tested). Variant G4: gains on the four separator-side nodes only (5zo's split), g<sub>i</sub> = 1 elsewhere. Forecasts at κ = 25.3, line through cycles 2..10, on 5zm's tables, no drift term, 5zs's q<sub>S</sub>: NS (5zu's cell 000, reproduced), NG = (G, q<sub>S</sub>), the primary, NG4 = (G4, q<sub>S</sub>), and 5zu's cell 100 (measured M<sub>w</sub>, q<sub>S</sub>; reproduced) as the ceiling. Lever error at cycle 99: |du(L<sub>99</sub>) − M<sub>w,99</sub>| in mV. Forecast error e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over 8, 12, 12, 8 designs.
  • Already seen: everything 5zk to 5zu report on these designs, including N's and the measured M<sub>w</sub> at cycles 10 and 99 (set medians), cells 000 and 100 and 5zo's node over-read at cycle 10. Not seen: any per-node gain, G or G4 at any cycle, NG or NG4 on any design. Risk named now: the gain is a straight-line scaling of a shift fitted over cycles in which s moves by under a tenth of its cycle-99 value, so a node whose lag grows or shrinks later is extrapolated wrongly, the same failure 5zq's drift line had.
  • H236 (the gain reads the OCP rise better): set median |G(L<sub>99</sub>) − M<sub>w,99</sub>| below N's on at least 3 of 4 sets. Refuted if on at most 1.
  • H237 (and carries OKane2022's forecast): set median e<sub>NG</sub> < e<sub>NS</sub> on OKane2022. Refuted if e<sub>NG</sub> > e<sub>NS</sub>.
  • H238 (half the OCP share): on OKane2022 set median e<sub>NG</sub> at most (e<sub>000</sub> + e<sub>100</sub>)/2 (halfway from NS to the measured-OCP ceiling). Refuted if above e<sub>000</sub>.
  • H239 (design by design): e<sub>NG</sub> < e<sub>NS</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • Reported, not hypothesised: set medians of g<sub>i</sub> by node (collector to separator), the plating-weighted mean gain, NG4's lever and forecast errors, and the counts NG<NS, NG4<NS, NG<NG4 per set.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zu, so a check on known designs, not a held-out test; the hypotheses lean on 5zo's and 5zu's directions; node OCPs and stoichiometries are model internals; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zu outcome: on OKane2022 the ten-cycle forecast's remaining error is the node lever's OCP part, not the drift; on Chen2020 it splits evenly between the two; the capacity factor's share is nil on every set. Of the gap between the best ten-cycle forecast and the all-measured diagnosis (6.7% against 1.5% on OKane2022), measuring the plating-weighted OCP rise buys 3.3 points (Shapley, set median) and the drift 1.1; on Chen2020 (5.4% against 1.4%) the two buy 2.1 and 2.0. On Ai2020 measuring the inputs makes the forecast worse (2.3% to 8.0%): there the node lever's errors cancel the law's. H232 and H234 supported, H233 and H235 inconclusive

  • Analysis: stdlib, 35 s (rows), report run once, nothing in experiments/budget/run.py changed after the plan. Reproduces 5zs, 5zt and 5zp: cell 000 equals NS, 010 equals ND and the all-measured cell 111 equals PQ (built 5zp's way, to 6 places) on all 40 designs, and each design's three Shapley values sum to its gap (tested).
  • H232 supported: on OKane2022 set median φ<sub>M</sub> = 0.033, φ<sub>D</sub> = 0.011, φ<sub>q</sub> = −0.001 (gap 0.056); M has the largest φ on 10 of 12 designs.
  • H233 inconclusive (rank 2 of 3): on Chen2020 φ<sub>M</sub> = 0.021, φ<sub>D</sub> = 0.020, φ<sub>q</sub> = −0.000 (gap 0.041); D has the largest φ on 7 of 12 designs, M on 4. The two are tied to within a point.
  • H234 supported (4 of 4 at most 0.01): set median φ<sub>q</sub> is −0.003, −0.000, −0.001, 0.003; measuring the factor raises the error on 6 of 8, 6 of 12, 7 of 12 and 2 of 8 designs.
  • H235 inconclusive: set median |I<sub>MD</sub>| is 0.002 on Chen2020 and 0.011 on OKane2022 (signed 0.002 and 0.000): on Chen2020 the lever and drift fixes add; on OKane2022 they interact design by design but with no common sign.
  • Reported: set median e by cell (000, 001, 010, 011, 100, 101, 110, 111): Ai2020 0.023, 0.020, 0.049, 0.063, 0.035, 0.040, 0.071, 0.080; Chen2020 0.054, 0.063, 0.024, 0.027, 0.039, 0.040, 0.017, 0.014; OKane2022 0.067, 0.069, 0.065, 0.058, 0.035, 0.041, 0.022, 0.015; NCA_Kim2011 0.030, 0.035, 0.030, 0.035, 0.010, 0.011, 0.010, 0.011. On NCA_Kim2011 the measured OCP rise alone (100) reaches the all-measured 1.0% (φ<sub>M</sub> 0.025 of a 0.028 gap; the drift is nil there, 5zt). On Ai2020 the gap is −0.069: φ<sub>M</sub> −0.020 (negative on 8 of 8 designs) and φ<sub>D</sub> −0.038 (6 of 8), so the forecast inputs' errors offset the law's line error and NS's 2.3% is partly luck, as 5zp found for its overpotential oracle (4.2 to 8.7%).
  • Reading: the one-input ceilings of 5zs and 5zt are confirmed and placed. The capacity factor is spent everywhere. What the ten-cycle forecast lacks on LG M50 is the path of the plating-weighted plating overpotential, and which half of it matters is set-dependent: its OCP part (the node lever's forecast of how the anode's local OCP rises at the plating nodes) on OKane2022, its OCP part and its non-OCP drift equally on Chen2020. 5zo already placed OKane2022's node-lever over-read at the separator half of the anode, so the next forecast to try is the node lever's OCP rise at the separator nodes, not another drift term. For a design search the advice is unchanged: fit the law's line through 30 to 50 cycles. Next: a ten-cycle forecast of the separator-side OCP rise (5zo's split) on OKane2022; why measured inputs make Ai2020 worse (the law's line, 5zo's bend); and the budget as the paper's error-budget table.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zt, so a decomposition on known designs, not a held-out test; H232 and H233 leaned on directions 5zo's O and 5zt's ND suggested; Shapley medians need not sum to the gap's median; M<sub>w</sub> and D<sub>w</sub> are model internals with cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/budget/results.txt, summary.json, rows.json, budget.svg; tests tests/test_budget.py.

2026-11-18 · Milestone 5zu: an error budget for the ten-cycle forecast. Of the gap between the best ten-cycle forecast (NS) and the all-measured diagnosis (PQ), how much is the node lever's OCP part, the non-OCP plating-overpotential drift and the capacity factor? (plan, written and committed before any of the new cells was computed; H232 to H235 are this entry's)

  • Question: 5zq to 5zt each tried a ten-cycle forecast of one input and measured it against a one-input ceiling: the factor (5zs's NM moves N by under a point on three sets), the drift (5zt's ND takes Chen2020 from 5.4 to 2.4% but OKane2022 only from 6.7 to 6.5%). One-at-a-time ceilings do not add when the error is an absolute log ratio and the inputs' errors offset, so they cannot say where OKane2022's 6.5% lives. A full factorial with a Shapley split does, and it is the error-budget table the paper needs.
  • Method, fixed now (experiments/budget/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs; 5zt's, 5zs's, 5zq's and 5zo's code imported unchanged). Three switches, each forecast (0) or measured (1): M = N's node-lever OCP rise (5zn) or the measured plating-weighted OCP rise M<sub>w</sub> (5zo's oracle); D = no drift (as NS) or the measured non-OCP drift D<sub>w</sub> = E<sub>w</sub> − M<sub>w</sub> (5zq, cycle-2 weights); q = 5zs's saturating ten-cycle factor q<sub>S</sub> or the measured factor q<sub>M</sub> (5zp). Eight cells mdq at κ = 25.3, line through cycles 2..10 on 5zm's tables; e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|. 000 is NS, 010 is ND, 111 is 5zp's PQ (M<sub>w</sub> + D<sub>w</sub> = E<sub>w</sub>; tested). Per design: Shapley values φ<sub>M</sub>, φ<sub>D</sub>, φ<sub>q</sub> of measuring each input (the drop in e; they sum to e<sub>000</sub> − e<sub>111</sub>), and the M–D interaction at q<sub>S</sub>, I<sub>MD</sub> = e<sub>110</sub> − e<sub>100</sub> − e<sub>010</sub> + e<sub>000</sub>. Set medians over 8, 12, 12, 8 designs.
  • Already seen: NS (000), ND (010) and PQ (111) on every design, and NM (N with q<sub>M</sub>, which is cell 001); 5zo's O (measured M<sub>w</sub> with the law's own factor, not q<sub>S</sub>: 0.042, 0.038, 0.034, 0.012) and 5zr's PE (measured E<sub>w</sub> with q<sub>E</sub>). So H232 and H233 lean on directions those suggest (O well below N on OKane2022; ND well below NS on Chen2020); what is new is the attribution with the other inputs measured, the factor's share in the presence of the others, and the interaction. Not seen: cells 100, 110, 011, 101 on any design, any Shapley value or interaction.
  • H232 (the OCP lever carries OKane2022): set median φ<sub>M</sub> is the largest of the three on OKane2022. Refuted if it is the smallest.
  • H233 (the drift carries Chen2020): set median φ<sub>D</sub> is the largest of the three on Chen2020. Refuted if it is the smallest.
  • H234 (the factor is spent): |set median φ<sub>q</sub>| at most 0.01 on at least 3 of 4 sets. Refuted if above 0.02 on 3 or more.
  • H235 (the inputs' errors offset): set median |I<sub>MD</sub>| at least 0.01 on both LG M50 sets. Refuted if below 0.005 on both.
  • Reported, not hypothesised: all eight cells' set medians, the gap e<sub>000</sub> − e<sub>111</sub>, signed I<sub>MD</sub>, and per set how many designs each input has the largest φ and how many it has a negative φ (measuring it makes the forecast worse on average).
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zt, so a decomposition on known designs, not a held-out test; Shapley medians need not sum to the gap's median; M<sub>w</sub> and D<sub>w</sub> are model internals with cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zt outcome: the drift forecast improves, the lithium-loss forecast does not. Tying the non-OCP plating-overpotential drift to the falling charge overpotential forecasts its cycle-99 value closer than 5zq's ten-cycle line on every set (set median error 3.5, 6.0, 4.9 mV against 13.0, 8.7, 7.1 on Ai2020, Chen2020, OKane2022), but fed to the node lever it is worse than no drift term on all four sets (7.6% against 5.4% on Chen2020, 7.9% against 6.7% on OKane2022) and beats the law's lever on 17 of 40 designs. The measured drift itself takes Chen2020 from 5.4 to 2.4% but OKane2022 only from 6.7 to 6.5%. H228 supported, H229 and H230 refuted, H231 inconclusive

  • Analysis: stdlib, 80 s (rows), report run once, nothing in experiments/etadrift/run.py changed after the plan. Reproduces 5zs and 5zq: A, N and NS equal 5zs's committed values on all 40 designs, and D<sub>10</sub>(L<sub>99</sub>) and D<sub>99</sub> equal 5zq's (tested).
  • H228 supported (4 of 4): set median |D<sub>η</sub>(L<sub>99</sub>) − D<sub>99</sub>| is 3.49 against the line's 12.98 mV (Ai2020), 6.00 against 8.71 (Chen2020), 4.85 against 7.09 (OKane2022), 0.02 against 0.02 (NCA_Kim2011, where the drift is nil; strictly lower in the unrounded medians).
  • H229 refuted (0 of 2): set median e<sub>FS</sub> against e<sub>NS</sub> is 0.076 against 0.054 (Chen2020) and 0.079 against 0.067 (OKane2022).
  • H230 refuted: FS beats A on 17 of 40 designs (4/8, 6/12, 4/12, 3/8).
  • H231 inconclusive (one set each way): e<sub>ND</sub> is 0.024 on Chen2020 (NS 0.054; ND beats NS on 11 of 12 designs) and 0.065 on OKane2022 (NS 0.067; 9 of 12).
  • Reported: FL (5zq's line with q<sub>S</sub>) is 0.067, 0.074, 0.095, 0.030; FH (the line held past cycle 10) is 0.017, 0.054, 0.075, 0.030, the best ten-cycle variant on Ai2020 (NS 0.023) and equal to NS on LG M50; FS beats FL on 31 of 40 designs but NS on only 12. ND on Ai2020 is 0.049 against NS's 0.023: there the measured drift makes the node lever worse, so N's OCP part already absorbs it. The held line is closer still to the measured cycle-99 drift than the tie (3.06, 3.35, 3.15 mV). The tie's ten-cycle slope k<sub>η</sub> is 0.082, 0.048, 0.029 mV of drift per mV of η fall; refitted over cycles 2..99 with the measured η (post hoc) it is 0.231, −0.043 and −0.057: on LG M50 the drift goes negative (−2.50, −2.58 mV at cycle 99) while η keeps falling, so the tie that holds over ten cycles has the wrong sign over the run, the risk the plan named.
  • Reading: on LG M50 every ten-cycle drift term tried (5zq's line, the held line, the η-tied drift) forecasts a positive drift at cycle 99 where the DFN gives a negative one, and adding it to the node lever makes the forecast worse in proportion to how much drift it adds; leaving it out (NS) or freezing it at cycle 10 (FH) is best. The ceiling splits the two LG M50 sets: on Chen2020 the measured drift takes the error from 5.4 to 2.4%, so the drift is the lever there and the ten cycles hold no sign of its turn-over; on OKane2022 it barely moves the error, so something else (the node lever's OCP part, or the law's form) carries its 6.5%. So the ten-cycle forecast's remaining error on LG M50 is not recoverable from a one-parameter tie to η, and is only half the drift. For a design search the advice is unchanged: fit the law's line through 30 to 50 cycles. Next: what sets the drift's turn-over on Chen2020 (the plating-overpotential split by node, whether it follows SEI growth at the separator), and why the measured drift leaves OKane2022 at 6.5%; 5zp's cycle-n weights on Ai2020 remain open.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zs; the tie is the simplest physically shaped drift (one slope), not the best possible; D is a model internal and η a symmetric cut-off shift (5zc), CC charge only; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/etadrift/results.txt, summary.json, rows.json, etadrift.svg; tests tests/test_etadrift.py.

2026-11-18 · Milestone 5zt: does tying the non-OCP plating-overpotential drift to the falling charge overpotential forecast it from cycles 2..10 better than 5zq's straight line, and does it carry the ten-cycle forecast on LG M50? (plan, written and committed before any of the new forecasts was computed; H228 to H231 are this entry's)

  • Question: 5zs closed the capacity factor (q<sub>S</sub> within 2.4 to 4.8% of the measured factor at cycle 99; the measured factor itself moves the node lever N by under a point on three sets) and left the ten-cycle forecast's error on LG M50 (5.4 to 7.6%) in the lever: the non-OCP part D of the plating-weighted plating overpotential, which 5zq's ten-cycle line forecast with the wrong sign at cycle 99 (+2.50 and +0.87 mV against −2.50 and −2.58) because D rises over cycles 2..10 and turns over later. 5zs named the next step: a physically shaped forecast of D tied to the charge overpotential η, which falls and levels off over the same range. Two questions: does a D that follows η's saturating fall forecast cycle-99 D better than the line, and is D the lever at all (N plus the measured D, ND, a ceiling that reads cycle 99)?
  • Method, fixed now (experiments/etadrift/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs, 5zs's, 5zq's and 5zp's code imported unchanged). D<sub>n</sub> = E<sub>w,n</sub> − M<sub>w,n</sub> as 5zq (cycle-2 weights, D<sub>2</sub> = 0). η<sub>S</sub> = 5zs's saturating ten-cycle fit, unchanged. Tie: D<sub>η</sub>(l) = k<sub>η</sub> (η<sub>S</sub>(L<sub>2</sub>) − η<sub>S</sub>(l)) for l > L<sub>2</sub>, with k<sub>η</sub> the least-squares slope through the origin of D<sub>n</sub> on η<sub>S</sub>(L<sub>2</sub>) − η<sub>S</sub>(L<sub>n</sub>), n = 2..10 (one parameter, no fit past cycle 10). Comparators: D<sub>10</sub>, 5zq's line (reproduced), and D<sub>10H</sub>, that line held at its L<sub>10</sub> value beyond. Forecasts at κ = 25.3, line through cycles 2..10, on 5zm's tables, all with 5zs's q<sub>S</sub>: A, N, NS (reproduced), FS = (N + D<sub>η</sub>, q<sub>S</sub>) the primary, FL = (N + D<sub>10</sub>, q<sub>S</sub>), FH = (N + D<sub>10H</sub>, q<sub>S</sub>), and ND = (N + measured D, q<sub>S</sub>; reads cycle 99, a diagnosis). Error e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over 8, 12, 12, 8 designs.
  • Already seen: everything 5zk to 5zs report on these designs, including 5zq's D at cycles 10 and 99 and D<sub>10</sub>(L<sub>99</sub>) (set medians), its F = (N + D<sub>10</sub>, q<sub>10</sub>), and 5zs's η<sub>S</sub>, q<sub>S</sub> and NS. Not seen: k<sub>η</sub>, D<sub>η</sub> or D<sub>10H</sub> at any cycle, and FS, FL, FH or ND on any design. The risk is named now: a tie to a monotone, levelling η can rise and level but cannot turn over, so on LG M50 it can at best shrink the over-read, not reach D's sign at cycle 99.
  • H228 (the tie beats the line in the drift): set median |D<sub>η</sub>(L<sub>99</sub>) − D<sub>99</sub>| below |D<sub>10</sub>(L<sub>99</sub>) − D<sub>99</sub>| on at least 3 of 4 sets. Refuted if on at most 1.
  • H229 (and carries the forecast on LG M50): set median e<sub>FS</sub> < e<sub>NS</sub> on both LG M50 sets (Chen2020, OKane2022). Refuted if on neither.
  • H230 (design by design): e<sub>FS</sub> < e<sub>A</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • H231 (the drift is the lever on LG M50): set median e<sub>ND</sub> at most 0.03 on both LG M50 sets. Refuted if above 0.05 on both.
  • Reported, not hypothesised: e of FL, FH, ND against A, N, NS, and design-by-design counts FS<A, FS<N, FS<NS, FS<FL, FH<NS, ND<NS; set medians of k<sub>η</sub>, the measured D at 10 and 99 and its largest-magnitude value, each forecast at L<sub>99</sub> and its error; and, post hoc, k<sub>η</sub> refitted over cycles 2..99 with the measured η, to show whether the tie holds along the run.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zs, so this is a check on known designs, not a held-out test; D is a model internal (plating overpotential at the nodes) and η a symmetric cut-off shift standing in for the charge overpotential (5zc), CC charge only; cycle-2 weights; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zs outcome: the capacity factor is done; the ten-cycle forecast's remaining error is the lever. A saturating ten-cycle fit of the charge overpotential brings the window factor to within 2.4 to 4.8% of the measured cycle-99 factor on all four sets (5zr's line: 3.6 to 7.6%), and the node lever fed the measured factor itself (NM, the ceiling) moves the cycle-99 lithium-loss error by at most 0.7 points on three sets (−0.2, +0.4, −0.7) and 1.3 on NCA_Kim2011. With the saturating factor the node lever beats the law's own lever on 22 of 40 designs. H224, H225 and H226 supported, H227 inconclusive

  • Analysis: stdlib, 19 s (rows), report run once, nothing in experiments/saturate/run.py changed after the plan. Reproduces 5zr: A, N, NE and q<sub>E</sub>'s error equal its committed values on all 40 designs (tested).
  • H224 supported (3 of 4): set median |ln(q<sub>S</sub>(L<sub>99</sub>)/q<sub>M</sub>(L<sub>99</sub>))| is 0.024 against q<sub>E</sub>'s 0.076 (Ai2020), 0.045 against 0.067 (Chen2020), 0.043 against 0.068 (OKane2022), 0.048 against 0.036 (NCA_Kim2011).
  • H225 supported (4 of 4 at most 0.05). q<sub>S</sub> reads 2.00, 1.45, 1.44 and 1.87 against measured 1.92, 1.54, 1.53 and 2.00.
  • H226 supported (3 of 4 at most 0.01, none above 0.02): set median e<sub>NM</sub> against e<sub>N</sub> is 0.020 against 0.023 (Ai2020), 0.063 against 0.059 (Chen2020), 0.069 against 0.076 (OKane2022), 0.035 against 0.048 (NCA_Kim2011); NM beats N on 4/8, 6/12, 8/12, 6/8 designs.
  • H227 inconclusive: NS beats A on 22 of 40 designs (6/8, 8/12, 5/12, 3/8), against NE's 14 in 5zr.
  • Reported: set median e<sub>NS</sub> is 0.023, 0.054, 0.067, 0.030 (A: 0.083, 0.082, 0.059, 0.022; N: 0.023, 0.059, 0.076, 0.048; NE: 0.028, 0.054, 0.081, 0.057); NS beats N on 2/8, 6/12, 8/12, 5/8 and NE on 6/8, 6/12, 5/12, 5/8. On NCA_Kim2011 NS (0.030) is below the measured-factor ceiling NM (0.035): factor errors and lever errors offset there, so a better factor is not always a better forecast. The hold q<sub>H</sub> is closer still to the measured factor on three sets (0.016, 0.031, 0.021, 0.059), but its forecast NH (0.022, 0.068, 0.076, 0.034) is no better than N on LG M50. AS (A's lever with q<sub>S</sub>) is 0.068, 0.098, 0.079, 0.016: the law's own lever with a better factor is worse on LG M50, as AE was in 5zr. η<sub>S</sub> at L<sub>99</sub> reads 120, 368, 373 and 163 mV against the 132, 372, 382 and 185 the cycle-99 charge needs (5zr's line 106, 341, 349, 155; the hold 143, 379, 390, 177). The fitted decay length is 1.3, 15.1, 4.1 and 0.74 times L<sub>10</sub> − L<sub>2</sub> (set medians), and 20 of 40 designs' λ sits on a grid end (2/8, 8/12, 6/12, 4/8), mostly the long end on LG M50, where the fit is close to 5zr's line.
  • Reading: three steps (5zq, 5zr, 5zs) took the ten-cycle forecast of the charge-capacity factor from 16 to 51% off at cycle 99 to 2.4 to 4.8% off, and NM shows that even the exact factor would change the node lever's cycle-99 error by under a point on three of four sets. So the capacity factor is no longer where the ten-cycle forecast's error lives. With N, the forecast is 2.3% off on Ai2020 and 3.0 to 4.8% on NCA_Kim2011, but 5.4 to 7.6% on LG M50, where 5zp's measured plating overpotential (with the measured factor) reached 1.4 to 1.5%: on LG M50 the error is the lever, the non-OCP part of the plating overpotential that 5zq's straight line could not follow (it rises, then turns over). For a design search the advice is unchanged: fit the law's line through 30 to 50 cycles. Next: a physically shaped ten-cycle forecast of the non-OCP plating-overpotential drift on LG M50 (for example tied to the falling charge overpotential η, which shares its turn-over), and 5zp's cycle-n weights on Ai2020.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zr; half the designs' decay lengths sit on a grid end, so the saturating fit is weakly determined and on LG M50 often a line; the hold variant was chosen after seeing 5zr's post hoc η; η is a symmetric cut-off shift (5zc), CC charge only; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/saturate/results.txt, summary.json, rows.json, saturate.svg; tests tests/test_saturate.py.

2026-11-18 · Milestone 5zs: does a saturating ten-cycle fit of the charge overpotential close the window factor's late under-read, and is any capacity-factor gain left for the node lever? (plan, written and committed before any of the new forecasts was computed; H224 to H227 are this entry's)

  • Question: 5zr's window factor q<sub>E</sub> forecast the cycle-99 charge-capacity factor within 3.6 to 7.6%, but its post hoc path showed the error opening late (−3.5 to −6.6% by cycles 75 to 99 on LG M50) because its ten-cycle η line keeps falling where the measured η levels off; and fed to the law with 5zn's node lever N it changed N's error by under 0.01. Two questions follow: does a saturating η (one whose fall levels off) close that late under-read from cycles 2..10 alone, and, more decisive for the programme, is there any capacity-factor gain left for N at all? The second is answered by N with the measured factor q<sub>M</sub> (NM, a ceiling that reads cycle 99): if NM is N to within 0.01, no forecast of the factor can help N, and the ten-cycle forecast's remaining error is the lever.
  • Method, fixed now (experiments/saturate/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs, 5zr's code imported unchanged). η<sub>n</sub> as 5zr, n = 2..10. Saturating fit η<sub>S</sub>(l) = c + d exp(−(l − L<sub>2</sub>)/λ): λ on a fixed grid of 60 log-spaced values from 0.25 to 20 times L<sub>10</sub> − L<sub>2</sub>, c and d by least squares for each λ, the λ with the least squared error kept (the long end of the grid is close to 5zr's line), clamped to [0, 0.49 (v<sub>hi</sub> − v<sub>lo</sub>)]. Hold η<sub>H</sub>(l): 5zr's line up to L<sub>10</sub>, held at its L<sub>10</sub> value beyond (no fit past the line). q<sub>S</sub>, q<sub>H</sub> = 5zr's window_factor with η<sub>S</sub>, η<sub>H</sub>. Forecasts at κ = 25.3, line through cycles 2..10, on 5zm's tables: A, N, NE (reproduced), NS, the primary (N's du, q<sub>S</sub>), NH (N, q<sub>H</sub>), AS (A's du, q<sub>S</sub>), and NM (N, q<sub>M</sub>; reads cycle 99, a diagnosis). Error e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over 8, 12, 12, 8 designs.
  • Already seen: everything 5zk to 5zr report on these designs, including 5zr's post hoc set medians of the η cycle 99 needs (132, 372, 382, 185 mV) against η at cycle 10 (144, 382, 392, 178): the hold variant was chosen knowing these, so it is reported, not hypothesised. Not seen: any saturating fit, q<sub>S</sub> or q<sub>H</sub> at any cycle, and NM, NS, NH or AS on any design.
  • H224 (saturation beats the line in the factor): set median |ln(q<sub>S</sub>(L<sub>99</sub>)/q<sub>M</sub>(L<sub>99</sub>))| below 5zr's |ln(q<sub>E</sub>/q<sub>M</sub>)| on at least 3 of 4 sets. Refuted if on at most 1.
  • H225 (and reaches it closely): set median |ln(q<sub>S</sub>/q<sub>M</sub>)| at cycle 99 at most 0.05 on at least 3 of 4 sets. Refuted if above 0.10 on 3 or more.
  • H226 (no capacity-factor gain is left for the node lever): set median |e<sub>NM</sub> − e<sub>N</sub>| at most 0.01 on at least 3 of 4 sets. Refuted if above 0.02 on 3 or more.
  • H227 (design by design): e<sub>NS</sub> < e<sub>A</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • Reported, not hypothesised: e of NH, AS, NM against A, N and NE, and design-by-design counts NS<A, NS<N, NS<NE, NH<N, NM<N, AS<A; set medians of q<sub>S</sub>, q<sub>H</sub> at L<sub>99</sub>, |ln(q<sub>H</sub>/q<sub>M</sub>)|, η<sub>S</sub> and η<sub>H</sub> at L<sub>99</sub> against the η cycle 99 needs, the fitted λ over L<sub>10</sub> − L<sub>2</sub>, and how many designs' λ sits on a grid end.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zr, so this is a check on known designs, not a held-out test; a three-parameter fit to nine points over a short range of lithium lost is weakly determined, which the grid-end count reports; η is a symmetric cut-off shift standing in for the charge overpotential (5zc), CC charge only; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zr outcome: yes for the factor, no for the forecast. The electrode-balance window with a ten-cycle line in the charge overpotential forecasts the cycle-99 charge-capacity factor within 3.6 to 7.6% on all four sets, where 5zq's straight line missed by 16 to 51%; but fed to the law with the node lever it beats 5zd's lever on only 14 of 40 designs (set medians 2.8% on Ai2020 against 8.3%, 5.4% on Chen2020 against 8.2%, 8.1% on OKane2022 against 5.9%, 5.7% on NCA_Kim2011 against 2.2%), and is no better than the node lever with the law's own factor. The balance alone, with η held, is closer still on three sets (2.4 to 4.0%). H220 and H221 supported, H222 inconclusive, H223 refuted

  • Analysis: stdlib, 18 s (rows), report run once, nothing in experiments/window/run.py changed after the plan apart from adding the posthoc command after the verdicts. Reproduces 5zq: A, N, NQ and PQ equal its committed values on all 40 designs (tested).
  • H220 supported (4 of 4 at most 0.10): set median |ln(q<sub>E</sub>(L<sub>99</sub>)/q<sub>M</sub>(L<sub>99</sub>))| is 0.076 (Ai2020), 0.067 (Chen2020), 0.068 (OKane2022), 0.036 (NCA_Kim2011); q<sub>E</sub> reads 1.86, 1.41, 1.40 and 1.87 against measured 1.92, 1.54, 1.53 and 2.00.
  • H221 supported (4 of 4): against 5zq's straight line's 0.512, 0.161, 0.157 and 0.232.
  • H222 inconclusive (2 of 4): set median e<sub>NE</sub> against e<sub>A</sub> is 0.028 against 0.083 (Ai2020), 0.054 against 0.082 (Chen2020), 0.081 against 0.059 (OKane2022), 0.057 against 0.022 (NCA_Kim2011).
  • H223 refuted: NE beats A on 14 of 40 designs (6/8, 5/12, 2/12, 1/8).
  • Reported: against the node lever with the law's factor (N: 0.023, 0.059, 0.076, 0.048) NE changes the set median by +0.005, −0.005, +0.005 and +0.009 and wins on 19 of 40 designs (2/8, 6/12, 7/12, 4/8), so the window factor adds nothing to N. AE (A's lever with q<sub>E</sub>) beats A on Ai2020 (0.068, 7/8) and NCA_Kim2011 (0.020, 6/8) and loses on LG M50 (0.101 and 0.094, 2/12 each). FE (5zq's F lever with q<sub>E</sub>) is 0.086, 0.082, 0.100, 0.057, no better than 5zq's F. PE (measured overpotential with q<sub>E</sub>, a diagnosis) is 0.060, 0.023, 0.034, 0.013 against PQ's 0.080, 0.014, 0.015, 0.011 and 5zp's P (law's factor) 0.087, 0.026, 0.029, 0.012: on Chen2020 the window keeps a quarter of what the measured factor gained over the law's (0.026 to 0.023, against PQ's 0.014), and on OKane2022 it loses ground (0.034 against 0.029). The balance alone (q<sub>B</sub>, η held at the law's ten-cycle mean, i.e. the law's own factor renormalised at L<sub>2</sub>) misses the measured factor at cycle 99 by 0.040, 0.034, 0.024 and 0.071, closer than q<sub>E</sub> on all but NCA_Kim2011. The effective charge overpotential falls with cycling on every set: η at cycles 2 and 10 is 151 and 144 mV (Ai2020), 388 and 382 (Chen2020), 397 and 392 (OKane2022), 196 and 178 (NCA_Kim2011), a ten-cycle slope of −0.57 to −1.20 mV per mmol lost; the line reads 106, 341, 349 and 155 mV at cycle 99, where the cycle-99 charge needs 132, 372, 382 and 185 (posthoc.txt). With the lines through 2..50, NE is 0.015, 0.035, 0.027, 0.012 and AE 0.026, 0.030, 0.017, 0.007, against A's 0.032, 0.020, 0.017, 0.011.
  • Post hoc (run.py posthoc, posthoc.txt, after the verdicts): along the path, on LG M50 q<sub>E</sub> stays within 1.1% of the measured factor to cycle 50 and falls to −3.5 to −6.6% by cycles 75 to 99, as the η line keeps falling where the measured η has levelled; q<sub>B</sub> over-reads by 2.2 to 5.1% from cycle 20 to 75 on LG M50 and by 2 to 4% on Ai2020 throughout. So the law's own factor is high by a few per cent in the middle of the run, the window with the η line is low by a few per cent at the end, and neither error is large.
  • Reading: the capacity factor's upward curve, which 5zq's straight line missed, is the open-circuit electrode balance: lost lithium slides the window along the two OCP curves, and that is nonlinear in lithium lost. The law already carries this through its own factor, which is within 2.4 to 7.1% of the measured one at cycle 99. So 5zq's "the capacity factor is the larger failure" was a failure of the straight line, not of the law, and resistance growth does not end the charge earlier in these runs: the effective charge overpotential falls by 6 to 18 mV over ten cycles and then levels. Getting the factor right to within a few per cent does not carry the forecast, though: NE is N to within 0.01 in set median, and PE keeps little or none of PQ's gain on LG M50, so the factor's last few per cent along the path still move cycle-99 lithium loss by one to two points. On LG M50 the ten-cycle forecast's remaining error is the lever: the law's du, where 5zp's measured plating overpotential took the error from 3.8 to 2.6% (Chen2020) before the factor mattered. For a design search the advice is unchanged: fit the law's line through 30 to 50 cycles (A<sub>50</sub> 1.1 to 3.2%). Next: a ten-cycle forecast of the plating-weighted plating overpotential's path from the node states (5zn's node lever applied to η<sub>pl</sub> rather than the node OCP, or a saturating fit of E<sub>w</sub>), and a saturating η (its fall levels off) in q<sub>E</sub>; 5zp's cycle-n weights on Ai2020 remain open.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zq; η is a symmetric cut-off shift standing in for the charge overpotential (5zc); CC charge only; 60-point window integration; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/window/results.txt, summary.json, posthoc.txt, rows.json, window.svg; tests tests/test_window.py.

2026-11-18 · Milestone 5zr: does the electrode-balance map, with a ten-cycle line in the charge overpotential, forecast the capacity factor that 5zq's straight line under-read? (plan, written and committed before any of the new forecasts was computed; H220 to H223 are this entry's)

  • Question: 5zq found that the measured charge-capacity factor q<sub>ch</sub>(2)/q<sub>ch</sub>(n) curves upward in lithium lost after cycle 10, so a ten-cycle straight line under-reads it at cycle 99 on every set (1.20 to 1.59 against 1.53 to 2.00), and named a physically shaped forecast as the next step: the constant-current charge shrinks because lost lithium slides and narrows the open-circuit window (5r's electrode-balance map, design only) and because a growing overpotential η ends the step earlier. Both are nonlinear in lithium lost through the OCP curves, so the map may bend where a line cannot. The question is whether the map, fed only a ten-cycle line in η, keeps the gain 5zp's measured factor gave.
  • Method, fixed now (experiments/window/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs, 5zq's, 5zp's and 5zc's code imported unchanged). Per cycle n = 2..10, η<sub>n</sub> = 5zc's solve_eta(n<sub>Li</sub> − L<sub>n</sub>, q<sub>ch</sub>(n)): the symmetric shift of both cut-offs that puts 5r's open-circuit window capacity at the measured constant-current charge Ah. Ten-cycle line η<sub>10</sub>(l) = a + s l, least squares on (L<sub>n</sub>, η<sub>n</sub>), n = 2..10, clamped to [0, 0.49 (v<sub>hi</sub> − v<sub>lo</sub>)] (as 5ze's η drift). Window factor q<sub>E</sub>(l) = Q<sub>η10(L2)</sub>(n<sub>Li</sub> − L<sub>2</sub>) / Q<sub>η10(l)</sub>(n<sub>Li</sub> − l) for l > L<sub>2</sub>, 1 below, with Q<sub>η</sub> 5zc's cap_eta. For comparison the balance alone, q<sub>B</sub>(l), the same with η held at the law's ten-cycle mean (the law's own factor renormalised at L<sub>2</sub>). Forecasts at κ = 25.3, line through cycles 2..10, on 5zm's tables: A and N (reproduced), NE, the primary (N's du, q<sub>E</sub>), AE (A's du, q<sub>E</sub>), FE (5zq's F du, N + D<sub>10</sub>, with q<sub>E</sub>), and PE (5zp's measured overpotential du<sub>P</sub> with q<sub>E</sub>; reads cycle 99, a diagnosis of whether q<sub>E</sub> can stand in for the measured factor in 5zp's PQ). Error e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over 8, 12, 12, 8 designs.
  • Already seen: everything 5zk to 5zq report on these designs (A, N, F, NQ, PQ, q<sub>M</sub> at cycle 99, q<sub>10</sub>, D, the curvatures), and the law's η as a ten-cycle mean of η<sub>n</sub>. Not seen: any η<sub>n</sub> series or η line on these designs, q<sub>E</sub> or q<sub>B</sub> at any cycle past 10, and any forecast built from them. 5ze fitted an η line on other pools (the levers read at η(l)), not as a capacity factor.
  • H220 (the window forecast reaches the measured factor): set median |ln(q<sub>E</sub>(L<sub>99</sub>)/q<sub>M</sub>(L<sub>99</sub>))| at most 0.10 on at least 3 of 4 sets. Refuted if above 0.25 on 3 or more (5zq's H218 bars).
  • H221 (it beats the straight line): set median |ln(q<sub>E</sub>/q<sub>M</sub>)| at cycle 99 below 5zq's |ln(q<sub>10</sub>/q<sub>M</sub>)| on at least 3 of 4 sets. Refuted if on at most 1.
  • H222 (and carries the forecast): set median e<sub>NE</sub> below e<sub>A</sub> on at least 3 of 4 sets. Refuted if on at most 1.
  • H223 (design by design): e<sub>NE</sub> < e<sub>A</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • Reported, not hypothesised: e of AE, FE, PE against A, N, NQ and PQ; NE and AE with the line through 2..30 and 2..50; set medians of η<sub>2</sub>, s (mV per mmol), q<sub>E</sub>(L<sub>99</sub>), q<sub>B</sub>(L<sub>99</sub>) and |ln(q<sub>B</sub>/q<sub>M</sub>)| at 99 (how much of the measured factor the balance alone explains); NE against N design by design.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zq, so this is a check on known designs, not a held-out test; η is a symmetric shift of both cut-offs standing in for the charge overpotential (5zc), and the constant-current charge ends at the upper cut-off only; open-circuit tables at 60-point integration; NE needs a cell model's node states at cycle 2 (for N), while AE needs only the design, the OCP curves and measured charge Ah; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zq outcome: no. Straight-line forecasts from cycles 2..10 of the two inputs 5zp fed by oracle keep little of its gain. With the node lever plus a ten-cycle drift line and a ten-cycle capacity-factor line (F), the ten-cycle forecast misses cycle-99 lithium loss by 5.7% on Chen2020 (5zd's lever A: 8.2%, oracle PQ: 1.4%), 7.2% on OKane2022 (A 5.9%), 10.1% on NCA_Kim2011 (A 2.2%) and 7.0% on Ai2020 (A 8.3%); F beats A on 15 of 40 designs. The capacity factor's line under-reads cycle 99 on every set (1.20 to 1.59 against 1.53 to 2.00), and the drift's line has the wrong sign at cycle 99 on both LG M50 sets. H217 refuted, H216, H218 and H219 inconclusive

  • Analysis: stdlib, 13 s (rows), report run once, nothing in experiments/drift/run.py changed after the plan. Reproduces 5zn and 5zp: A, N and PQ equal the committed values on all 40 designs (difference 0.0, tested).
  • H216 inconclusive (2 of 4): set median e<sub>F</sub> against e<sub>A</sub> is 0.057 against 0.082 (Chen2020), 0.070 against 0.083 (Ai2020), 0.072 against 0.059 (OKane2022), 0.101 against 0.022 (NCA_Kim2011).
  • H217 refuted: F beats A on 15 of 40 designs (4/8, 8/12, 2/12, 1/8).
  • H218 inconclusive (none at most 0.10, one above 0.25): set median |ln(q<sub>10</sub>(L<sub>99</sub>)/q<sub>M</sub>(L<sub>99</sub>))| is 0.161 (Chen2020), 0.157 (OKane2022), 0.232 (NCA_Kim2011), 0.512 (Ai2020). The line under-reads on every set: forecast 1.35, 1.34, 1.59 and 1.20 against measured 1.54, 1.53, 2.00 and 1.92. The charge-capacity factor curves upward in lithium lost after cycle 10.
  • H219 inconclusive (2 within a quarter of |M<sub>w,99</sub>|, none above half): set median |D<sub>10</sub>(L<sub>99</sub>) − D<sub>99</sub>| is 8.71 mV against |M<sub>w,99</sub>| 30.5 (Chen2020), 7.09 against 29.8 (OKane2022), 0.02 against 128.9 (NCA_Kim2011, where the drift is nil), 12.98 against 46.6 (Ai2020). On LG M50 the line forecasts +2.50 and +0.87 mV at cycle 99 where the DFN gives −2.50 and −2.58: the risk the plan named. The drift rises over cycles 2..10 (0.56 and 0.26 mV at cycle 10) and turns over later.
  • Reported: AQ (A's lever with q<sub>10</sub>) is worse than A on three sets (0.150 against 0.082 on Chen2020, 0.128 against 0.059 on OKane2022, 0.060 against 0.083 on Ai2020 the exception); NQ 0.055 and 0.068 on LG M50, close to F; G (E<sub>w</sub>'s own ten-cycle line with q<sub>10</sub>) is the best ten-cycle variant on LG M50 (0.053, 0.055) and the worst on the other two (0.121, 0.159). F beats N on 10 of 40 (1/8, 3/12, 6/12, 0/8). The share of the A-to-PQ gap F closes is 0.37 on Chen2020 and −0.30 on OKane2022 (on Ai2020 and NCA_Kim2011 PQ is not much better than A, so the share is meaningless there: 4.35 and −6.94). F with the line through 2..30 and 2..50 (the input fits kept on 2..10): 0.043/0.030 (Chen2020), 0.049/0.032 (OKane2022), 0.056/0.035 (NCA_Kim2011), 0.063/0.040 (Ai2020), against A's 0.046/0.020, 0.028/0.017, 0.013/0.011, 0.039/0.032: a longer line does not rescue the inputs' ten-cycle fits. Set median |c<sub>F</sub>| is 0.17 to 0.29 on three sets and 0.86 on NCA_Kim2011, against PQ's 0.03 to 0.24.
  • Reading: 5zp's diagnosis stands (the law's form is close to right on LG M50 when fed the two measured inputs), but the inputs themselves are not linear in lithium lost over the first ten cycles' range, so ten cycles cannot hand them to the law by a straight line. The capacity factor is the larger failure: it accelerates after cycle 10 on every set, and a line that under-reads it makes A's forecast worse, not better, because A's own law-side factor already rises faster. The drift is small (under 5 mV at cycle 99 against 30 to 130 mV of OCP rise) but enters the exponent at 25.3 V<sup>−1</sup>, and its turn-over means any early extrapolation over-reads it. For a design search 5zm's advice still holds: fit the law's line through 30 to 50 cycles. The next step is a physically shaped forecast of the capacity factor: q<sub>ch</sub> falls as lithium loss shrinks the window and as resistance growth ends the constant-current step earlier, and 5r's electrode-balance map already gives the first part from the design alone; fed that map's q(L) in place of q<sub>10</sub>, does the forecast keep PQ's gain?
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zp; cycle-2 weights; end-of-charge values only; η<sub>pl</sub> and node OCPs are model internals; through-origin straight lines are the simplest forecasts, not the best possible ones; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/drift/results.txt, summary.json, rows.json, drift.svg; tests tests/test_drift.py.

2026-11-18 · Milestone 5zq: can cycles 2..10 forecast the two inputs 5zp fed by oracle? A ten-cycle forecast of the non-OCP plating-overpotential drift and the charge-capacity factor, against 5zd's and 5zn's levers (plan, written and committed before any of the new forecasts was computed; H216 to H219 are this entry's)

  • Question: 5zp found that on LG M50 the law's straight line in R against cycle number holds to |c| of 0.03 to 0.04 when it is fed the measured plating overpotential and the measured charge-capacity factor (PQ, ten-cycle error 1.4 and 1.5%), and that "what a ten-cycle forecast lacks there is a forecast of those two, not a different law". PQ reads cycle 99. This step asks whether the simplest forecasts of the two that read only cycles 2..10 keep enough of PQ's gain to beat the levers a ten-cycle forecast can actually use (5zd's A and 5zn's node lever N).
  • Method, fixed now (experiments/drift/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs, 5zp's and 5zo's code imported unchanged). D<sub>n</sub> = E<sub>w,n</sub> − M<sub>w,n</sub>, the non-OCP part of the plating-weighted plating-overpotential rise from cycle 2 (5zp's E<sub>w</sub> less 5zo's M<sub>w</sub>, cycle-2 weights; D<sub>2</sub> = 0). Ten-cycle drift D<sub>10</sub>(l) = k<sub>D</sub>(l − L<sub>2</sub>) for l > L<sub>2</sub>, 0 below, k<sub>D</sub> the least-squares slope through the origin of D<sub>n</sub> on L<sub>n</sub> − L<sub>2</sub>, n = 2..10. Ten-cycle capacity factor q<sub>10</sub>(l) = 1 + k<sub>q</sub>(l − L<sub>2</sub>) for l > L<sub>2</sub>, 1 below, k<sub>q</sub> the same fit of q<sub>ch</sub>(2)/q<sub>ch</sub>(n) − 1, n = 2..10. Forecasts at κ = 25.3, line through cycles 2..10, on 5zm's tables: A (5zd's lever, law's capacity factor; reproduced), N (5zn's node lever, law's factor; reproduced), F, the primary (du = N + D<sub>10</sub>, q<sub>10</sub>), AQ (A's du, q<sub>10</sub>), NQ (N, q<sub>10</sub>), G (du = E<sub>10</sub>(l) = k<sub>E</sub>(l − L<sub>2</sub>), the same through-origin fit of E<sub>w,n</sub> itself, q<sub>10</sub>), and PQ (5zp's diagnosis, reproduced). Error e = |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; set medians over 8, 12, 12, 8 designs. Only PQ reads past cycle 10.
  • Already seen: everything 5zk to 5zp report on these designs (A, N, O, P, OQ, PQ, E and M at cycles 10 and 99, q<sub>ch</sub>(2)/q<sub>ch</sub>(99), the curvatures). Not seen: any fit over cycles 2..10 of D, E or the capacity factor, and any forecast built from one.
  • H216 (the ten-cycle forecast of both inputs beats the law's lever): set median e<sub>F</sub> below e<sub>A</sub> on at least 3 of 4 sets. Refuted if on at most 1.
  • H217 (design by design): e<sub>F</sub> < e<sub>A</sub> on at least 26 of 40 designs (one-sided sign test p ≈ 0.04). Refuted if on at most 20.
  • H218 (the capacity factor extrapolates): set median |ln(q<sub>10</sub>(L<sub>99</sub>)/q<sub>M</sub>(L<sub>99</sub>))| at most 0.10 on at least 3 of 4 sets. Refuted if above 0.25 on 3 or more.
  • H219 (the drift extrapolates): set median |D<sub>10</sub>(L<sub>99</sub>) − D<sub>99</sub>| at most a quarter of the set median |M<sub>w,99</sub>| on at least 3 of 4 sets. Refuted if above half of it on 3 or more. (5zp's E/M of 0.91 to 1.10 at cycle 99 against E above M at cycle 10 suggests D changes sign on LG M50, which a line through the origin cannot follow; that is the risk this tests.)
  • Reported, not hypothesised: e of AQ, NQ, G against A, N, F and PQ; F against N design by design; F with the line through cycles 2..30 and 2..50 (the fits of D and q kept on 2..10); k<sub>D</sub> and k<sub>q</sub> set medians; the share of the A-to-PQ gap F closes, (e<sub>A</sub> − e<sub>F</sub>)/(e<sub>A</sub> − e<sub>PQ</sub>) on set medians.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zp, so this is a check on known designs, not a held-out test; cycle-2 weights; end-of-charge values only; η<sub>pl</sub> and node OCPs are model internals, so F needs a cell model's node states at cycles 2..10, while q<sub>10</sub> needs only measured charge capacity; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only. 5zp's other next step (cycle-n weights on Ai2020) is left for a later step.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zp outcome: on LG M50 the law's line bends because it holds two things at cycle 2, the non-OCP part of the plating overpotential and the capacity factor; fed both as the DFN measured them, the ten-cycle forecast misses cycle-99 lithium loss by 1.4% (Chen2020) and 1.5% (OKane2022) against 5zo's 3.8 and 3.4%, and the line's bend falls from 0.10 and 0.087 to 0.030 and 0.038. Either alone does little, and on Ai2020 the overpotential makes it worse (bend 0.13 to 0.27, error 4.2 to 8.7%). The bend is not 5zm's coarse table. H212 supported (narrowly), H213 and H214 inconclusive, H215 supported

  • Analysis: stdlib, 26 s (rows), report run once, nothing in experiments/rate/run.py changed after the plan. Reproduces 5zo: O's error and curvature equal 5zo's committed values on all 40 designs (tested).
  • H212 supported (3 of 4), but the third set carries no information: set median |c<sub>P</sub>| against |c<sub>O</sub>| is 0.080 against 0.100 (Chen2020), 0.080 against 0.087 (OKane2022), 0.1085 against 0.1086 (NCA_Kim2011, where the plating overpotential's rise equals the OCP's, E/M = 1.00 at cycle 99, so P is O) and 0.271 against 0.133 (Ai2020).
  • H213 inconclusive (2 of 4): e<sub>P</sub> against e<sub>O</sub> 0.026 against 0.038 (Chen2020), 0.029 against 0.034 (OKane2022), 0.012 against 0.012 (NCA_Kim2011, 0.01240 against 0.01234), 0.087 against 0.042 (Ai2020). Design by design P beats O on 8/12, 7/12, 3/8, 2/8.
  • H214 inconclusive (2 of 4): the measured capacity factor alone lowers |c| on Ai2020 (0.117) and NCA_Kim2011 (0.070) and raises it on both LG M50 sets (0.118, 0.100): it flips the bend's sign there (signed c 0.020 to −0.063 on Chen2020, 0.065 to −0.042 on OKane2022).
  • H215 supported: the 600-cell table moves set median |c<sub>O</sub>| by 0.001, 0.002, 0.004 and 0.000; errors move by at most 0.002.
  • Reported: PQ, both measured, gives e 0.014 (Chen2020), 0.015 (OKane2022), 0.011 (NCA_Kim2011), 0.080 (Ai2020) and |c| 0.030, 0.038, 0.069, 0.239; PQ beats O on 9/12, 9/12, 6/8, 2/8 designs. On LG M50 that ten-cycle error matches what 5zo needed a fifty-cycle line for (O<sub>50</sub> 0.016, 0.015). P's line through 30 and 50 cycles: 0.017/0.013 (Chen2020), 0.019/0.014 (OKane2022), 0.012/0.010 (NCA_Kim2011), 0.049/0.024 (Ai2020). The plating-overpotential rise against the OCP rise at cycle 99 (E/M) is 0.92 and 0.91 on LG M50, 1.00 on NCA_Kim2011, 1.10 on Ai2020; at cycle 10 E exceeds M on every set but NCA_Kim2011 (3.27 against 2.88 mV on Chen2020). The measured capacity factor q<sub>ch</sub>(2)/q<sub>ch</sub>(99) is 1.53 to 2.00.
  • Reading: on LG M50 the two held inputs pull the bend opposite ways, so each alone moves it little or past zero. Given the law's capacity factor, the measured overpotential leaves the signed set-median bend positive (0.067 on Chen2020, 0.066 on OKane2022); the measured capacity factor alone pushes it negative (−0.063, −0.042); with both it is −0.009 and 0.001. The plating overpotential rises faster than the OCP over the first ten cycles (3.27 against 2.88 mV on Chen2020) and slower by cycle 99 (E/M 0.92); how each moves R's early and late slopes is not decomposed here. With both, the law's straight line holds to |c| of 0.03 to 0.04, and a ten-cycle line is as good as 5zo's fifty-cycle one. So the law's rate form, R(L) = ∫ exp(κ du) Q<sub>0</sub>/Q dl, is close to right on LG M50 when du is the full plating overpotential and Q the delivered charge; what a ten-cycle forecast lacks there is a forecast of those two, not a different law. Ai2020 is the exception: its overpotential rises 10% more than its OCP by cycle 99 and feeding that in doubles the bend, so on that set something else (the plating's location moving off its cycle-2 weights, 5zk, is the first suspect) offsets it. Next: forecast the non-OCP overpotential drift and the charge-capacity factor from cycles 2..10 (for example the resistance growth rate times the charge current), and test cycle-n weights on Ai2020.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zo; cycle-2 weights; end-of-charge values only; η<sub>pl</sub> and node OCPs are model internals; P, OQ, PQ read cycle 99 by construction and are diagnoses; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/rate/results.txt, summary.json, rows.json, rate.svg; tests tests/test_rate.py.

2026-11-18 · Milestone 5zp: does the law's line bend because it holds the plating overpotential's non-OCP part, or the capacity factor, at cycle 2? An overpotential oracle, a measured-capacity oracle and a grid check on 5zo's bend (plan, written and committed before any of the new forecasts or curvatures was computed; H212 to H215 are this entry's)

  • Question: 5zo found that even fed the measured plating-weighted OCP rise (oracle O), the law's line in R against cycle number bends by c = ln(s<sub>late</sub>/s<sub>early</sub>) of 0.09 to 0.13 in set-median size, which leaves 1.2 to 4.2% of the ten-cycle forecast's error, and named the law's rate form as the next suspect. With du set to the measured OCP rise, two inputs of the law are still held at their cycle-2..10 form: (a) the kinetic driving force, which the law takes to rise only by the OCP rise, while the plating reaction overpotential also moves with the intercalation overpotential and film drop as resistance grows; (b) the capacity factor Q<sub>η</sub>(0)/Q<sub>η</sub>(L), computed on a window shortened by an η fixed from cycles 2..10. 5zk's records hold the end-of-charge plating reaction overpotential of every node on every cycle (eta_pl_node, never used so far) and each cycle's charge time, so both can be replaced by what the DFN did. One more candidate is ours: 5zm's tables put about two of 60 cells inside cycles 2..10, so part of c may be the grid.
  • Method, fixed now (experiments/rate/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs, 5zo's code imported unchanged). E<sub>w,n</sub> = Σ w<sub>i</sub>(2) (η<sub>pl,i</sub>(n) − η<sub>pl,i</sub>(2)), the plating-weighted rise of the end-of-charge plating overpotential from cycle 2 at cycle-2 weights (5zl's weighting, with η<sub>pl</sub> in place of the node OCP). Lever du<sub>P</sub>: 5zo's oracle_du on the points (L<sub>n</sub>, E<sub>w,n</sub>), n = 2..99. Measured capacity factor q<sub>M</sub>(l): linear through (L<sub>n</sub>, q<sub>ch</sub>(2)/q<sub>ch</sub>(n)), n = 2..99, q<sub>ch</sub> the constant-current charge Ah; 1 below L<sub>2</sub> (a constant factor there shifts R by a constant the intercept absorbs); beyond L<sub>99</sub> the least-squares slope over n = 90..99. Forecasts at κ = 25.3, line through cycles 2..10, on 5zo's tables: O (du<sub>O</sub>, law's qr; 5zo's, reproduced), P (du<sub>P</sub>, law's qr), OQ (du<sub>O</sub>, q<sub>M</sub>), PQ (du<sub>P</sub>, q<sub>M</sub>), and O<sub>fine</sub> (O on the same span with 600 cells instead of 60). Curvature c as 5zo (curvature). Error |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|. Set medians over 8, 12, 12, 8 designs. All of P, OQ, PQ read cycle 99: diagnoses, not forecasts.
  • Already seen: everything 5zk to 5zo report on these designs (A, N, O, W, c<sub>O</sub>, node OCPs, plating shares, charge times as they enter q<sub>ch</sub> in η). Not seen: any η<sub>pl</sub> series, any forecast or curvature with du<sub>P</sub> or q<sub>M</sub>, any table finer than 60 cells. Before writing this plan one cycle-2 η<sub>pl</sub> row of one design was printed to fix the sign (positive at the collector, where nothing plates, and negative next to the separator), nothing else.
  • H212 (the driving force straightens the line): set median |c<sub>P</sub>| below set median |c<sub>O</sub>| on at least 3 of 4 sets. Refuted if on at most 1.
  • H213 (and carries the forecast): set median e<sub>P</sub> below e<sub>O</sub> on at least 3 of 4 sets. Refuted if on at most 1.
  • H214 (the capacity factor bends the line): set median |c<sub>OQ</sub>| below |c<sub>O</sub>| on at least 3 of 4 sets. Refuted if on at most 1.
  • H215 (the bend is not the grid): |set median |c<sub>O,fine</sub>| − set median |c<sub>O</sub>|| at most 0.02 on all 4 sets. Refuted if above 0.05 on 2 or more.
  • Reported, not hypothesised: PQ's error and |c|; P with the line through 2..30 and 2..50; the signed set-median c of each variant; the set-median ratio E<sub>w,99</sub>/M<sub>w,99</sub> (how much of the driving-force rise is the OCP); e and c of P on the fine grid.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zo; cycle-2 weights; end-of-charge values only, while plating runs over the late part of each charge; η<sub>pl</sub> and node OCPs are model internals; all variants read cycle 99 by construction; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-18 · Milestone 5zo outcome: about half of the ten-cycle forecast's error on LG M50 is the lever's and half is the law's line. Fed the measured plating-weighted OCP rise (an oracle lever that reads every cycle), the forecast at 25.3 with its line through cycles 2..10 misses cycle-99 lithium loss by 3.8% on Chen2020, 3.4% on OKane2022, 1.2% on NCA_Kim2011 and 4.2% on Ai2020, against 8.2, 5.9, 2.2 and 8.3% for 5zd's lever; the R slope still drifts by 9 to 13% between cycles 2..10 and 50..99 with the true lever. The node lever's OKane2022 over-read sits at the separator, not the collector (collector half's share 0.21; 0 of 12 designs). H209 supported, H210 inconclusive, H211 refuted

  • Analysis: stdlib, 19 s (rows), report run once, nothing in experiments/oracle/run.py changed after the plan apart from adding the posthoc command after the verdicts. Reproduces 5zn: A, N and W equal 5zn's committed values on all 40 designs (tested).
  • H209 supported (3 of 4): set median error of O against A and N is 0.038 against 0.082 and 0.059 (Chen2020), 0.034 against 0.059 and 0.076 (OKane2022), 0.012 against 0.022 and 0.048 (NCA_Kim2011); on Ai2020 O's 0.042 halves A's 0.083 but loses to N's 0.023. Design by design O beats both on 18 of 40 (0/8, 9/12, 5/12, 4/8).
  • H210 inconclusive (1 at most 0.10, none above 0.25): set median |c| is 0.133 (Ai2020), 0.1000 (Chen2020, 0.10002, over the line by rounding), 0.087 (OKane2022), 0.109 (NCA_Kim2011). Signed set medians are 0.13, 0.02, 0.06 and 0.01: the drift is design by design and of either sign on three sets, positive (the rate in R accelerating) on Ai2020.
  • H211 refuted (0 of 12): on OKane2022 all 12 designs have a positive cycle-10 over-read (set median 2.29 mV, collector half 0.49), and the collector half's share is 0.21.
  • Reported: O with its line through 30 and 50 cycles is 0.029 and 0.014 (Ai2020), 0.031 and 0.016 (Chen2020), 0.023 and 0.015 (OKane2022), 0.012 and 0.010 (NCA_Kim2011), against A's 0.039/0.032, 0.046/0.020, 0.028/0.017, 0.013/0.011: the true lever helps most where the line is short. 5zl's W (A's lever at κ<sub>w</sub>, also reading cycle 99) beats O on LG M50 (0.025 and 0.019) because its exponent is fitted to the whole path and so absorbs some of the line's drift; they tie on NCA_Kim2011 (0.012). The node split on the other sets: the collector half's share of a positive over-read is 0.21 (Ai2020) and 0.12 (Chen2020); NCA_Kim2011's over-read is negative on 4 of 8 designs. The per-node Spearman of (P<sub>i</sub> − M<sub>i</sub>) on x<sub>i</sub>(2) is −0.07, −0.35, −0.30, −0.41: unweighted, the node lever over-reads the low-stoichiometry (collector-side) nodes more, but little plating sits there.
  • Post hoc (run.py posthoc, posthoc.txt, after the verdicts): x<sub>i</sub>(2) rises from the collector to the separator on every set (OKane2022 0.39 to 0.68), and the four separator-side nodes carry 0.56 of OKane2022's positive over-read (0.74 on Ai2020, 0.27 on Chen2020). So 5zn's suspect was the right nodes by stoichiometry but the wrong ones by weight: the over-read that matters is where the plating is, at the deepest-lithiated nodes next to the separator.
  • Reading: the two parts 5zn named are about equal on LG M50. A perfect plating-weighted lever takes the ten-cycle error from 8.2 to 3.8% on Chen2020 and from 5.9 to 3.4% on OKane2022; what is left is the law's straight line in R against cycle number, whose slope moves by about 10% across the run even with the true lever, and no lever read from cycle 2 can remove that. On Ai2020 the node lever beats the oracle, so its 5zn win there is partly an under-read early (ρ<sub>node,10</sub> 0.67) cancelling the line's positive drift (c = +0.13), not a better lever. For a design search, 5zm's advice holds and is now explained: fitting the line through 30 to 50 cycles buys more than any lever on LG M50. The next step is the law's rate form: test whether c follows the drift of the end-of-charge overpotential η (the law holds η at its cycles-2..10 value while resistance grows) or the capacity factor Q<sub>0</sub>/Q.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zn; cycle-2 weights; end-of-charge node OCPs are a model internal; the oracle reads cycle 99 by construction; R tables with about two cells inside cycles 2..10 (5zd's span); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/oracle/results.txt, summary.json, posthoc.txt, rows.json, oracle.svg; tests tests/test_oracle.py.

2026-11-18 · Milestone 5zo: is the ten-cycle forecast's remaining error in the lever or in the law's constant-rate line? An oracle-lever decomposition, and a node-by-node split of the OKane2022 over-read (plan, written and committed before any oracle forecast, curvature or node split was computed; H209 to H211 are this entry's)

  • Question: 5zn found the node lever reads the plating-weighted rise right by cycle 99 on three sets but the ten-cycle forecast at 25.3 still misses by 0.02 to 0.08, and that the miss has "a second part outside the lever's level: its shape beyond the first ten cycles' range". Two places can hold that part. Either the lever (any lever read from cycle 2) mis-predicts the rise far from cycle 10, or the law itself, a straight line in R(L) = ∫ exp(κ du) Q<sub>0</sub>/Q dl against cycle number, bends even when its du is the true plating-weighted rise. Feeding the law the measured rise (an oracle lever that reads every cycle) separates the two: if the oracle forecast is accurate from ten cycles, the residual is the lever's; if it is not, no better lever will fix the forecast and the law's rate form is next. 5zn also left open why the node lever over-reads OKane2022's early rise (5.49 against 3.00 mV at cycle 10); its named suspect is the nodes nearest the current collector, whose x<sub>i</sub>(2) is lowest.
  • Method, fixed now (experiments/oracle/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs in depth/bench.jsonl, 5zn's balance, η, tables, node lever and forecast code imported unchanged). Oracle lever du<sub>O</sub>(l): linear interpolation of the points (L<sub>n</sub>, M<sub>w,n</sub>), n = 2..99, with M<sub>w,2</sub> = 0 (5zl's plating-weighted end-of-charge OCP rise from cycle 2 at cycle-2 weights), du<sub>O</sub> = 0 below L<sub>2</sub> (a constant there only shifts R by a constant, which the line's intercept absorbs), and beyond L<sub>99</sub> extended with the least-squares slope of M<sub>w</sub> on L over n = 90..99. Forecast O = 5zf's forecast at κ = 25.3, line through cycles 2..10, with 5zm's tables and du replaced by du<sub>O</sub>; it reads cycle 99, so it is a diagnosis, the best any lever can give this law. Curvature: on O's R table, s<sub>early</sub> = least-squares slope of R<sub>O</sub>(L<sub>n</sub>) on n over n = 2..10, s<sub>late</sub> over n = 50..99, c = ln(s<sub>late</sub>/s<sub>early</sub>) (0 for a law whose line holds). Node split at cycle 10: per node i, the node lever's predicted rise P<sub>i</sub> = U<sub>n</sub>(x<sub>i</sub>(2) + s(L<sub>10</sub>)) − U<sub>n</sub>(x<sub>i</sub>(2)) against the measured M<sub>i</sub> = u<sub>i</sub>(10) − u<sub>i</sub>(2), weighted over-read o<sub>i</sub> = w<sub>i</sub>(2)(P<sub>i</sub> − M<sub>i</sub>); the collector half is nodes 1 to 10 of 20 (x_n from the collector), and its share is Σ<sub>collector</sub> o<sub>i</sub> / Σ<sub>all</sub> o<sub>i</sub>, taken only where the total is positive. A and N are 5zn's (5zd's lever and the node lever at 25.3, line through 2..10). Error |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|, set medians over 8, 12, 12, 8 designs.
  • Already seen: every quantity 5zk to 5zn report on these designs (A, N, the one-point variant, 5zl's κ<sub>w</sub> forecast W, ρ<sub>node,k</sub>, set-median rises at cycle 10). Not seen: any forecast with du<sub>O</sub>, any R curvature, any node-resolved over-read.
  • H209 (the residual is the lever's): O's set median error is below both A's and N's on at least 3 of 4 sets. Refuted if on at most 1 (then the law's line, not the lever, holds most of the ten-cycle miss).
  • H210 (the law's line holds given the true lever): set median |c| at most 0.10 on at least 3 of 4 sets. Refuted if above 0.25 on 3 or more.
  • H211 (OKane2022's over-read sits at the collector): on OKane2022, among designs with a positive total over-read at cycle 10, the collector half carries more than half of it on at least two thirds. Refuted if on at most one third.
  • Reported, not hypothesised: O with the line through cycles 2..30 and 2..50; O against W (both read cycle 99); the sign of c per set; the node split on all four sets; the per-design Spearman of (P<sub>i</sub> − M<sub>i</sub>) on x<sub>i</sub>(2) across the 20 nodes, set medians.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zn; cycle-2 weights; end-of-charge node OCPs are a model internal; 5zm's R tables put only about two of their 60 cells inside cycles 2..10 (5zd's span, kept so O compares with A and N), so O inherits that resolution; the oracle reads cycle 99 by construction and is not a forecast; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zn outcome: the plateau explains the measured rise but not the forecast. Read at each node's cycle-2 stoichiometry, the law's uniform shift reproduces the plating-weighted OCP rise to within 2 to 16% by cycle 99 on three sets (slope 1.00 Ai2020, 0.98 Chen2020, 1.18 NCA_Kim2011; 0.84 OKane2022), against the law's own lever's 1.35 to 1.49 on LG M50, and on Chen2020 its rise from cycle 2 to 10 is 3.25 mV against 2.88 measured and 0.42 for the law. But the ten-cycle forecast at the physical exponent with this lever beats 5zd's on 2 of 4 sets (Ai2020 0.083 to 0.023, Chen2020 0.082 to 0.059) and loses on OKane2022 and NCA_Kim2011 (0.059 to 0.076, 0.022 to 0.048); 22 of 40 designs. H204 to H208 all inconclusive

  • Analysis: stdlib, 16 s (rows), report run once, nothing in experiments/plateau/run.py changed after the plan was committed. Reproduces 5zm and 5zl: A's set medians (0.083, 0.082, 0.059, 0.022) and 5zl's error at κ<sub>w</sub> (0.085, 0.025, 0.019, 0.012) equal the committed values. A test checks that the node lever equals 5zd's lever when every node sits at the window top.
  • H204 inconclusive (2 at most 0.15, none above 0.3): set median |ln ρ<sub>node,99</sub>| 0.024 (Ai2020), 0.095 (Chen2020), 0.221 (OKane2022), 0.167 (NCA_Kim2011).
  • H205 inconclusive (2 at most 0.3, none above 0.6): |ln ρ<sub>node,10</sub>| 0.409, 0.220, 0.556, 0.160. The ratio still drifts with k (set medians ρ<sub>node,k</sub> at k = 10, 30, 99: Ai2020 0.67, 0.91, 1.00; Chen2020 0.81, 0.85, 0.98; OKane2022 0.57, 0.65, 0.84; NCA_Kim2011 0.99, 1.08, 1.18), but far less than 5zm's law-lever ratio (25.3 × ratio 148 to 30 on Chen2020, a factor of 5; here 1.2).
  • H206 inconclusive (2 of 4): N against A 0.023 against 0.083 (Ai2020), 0.059 against 0.082 (Chen2020), 0.076 against 0.059 (OKane2022), 0.048 against 0.022 (NCA_Kim2011).
  • H207 inconclusive: N beats A on 22 of 40 designs (7/8, 9/12, 5/12, 1/8; one-sided sign test p = 0.32).
  • H208 inconclusive: N over 5zl's diagnostic error is 2.41 (Chen2020) and 3.93 (OKane2022).
  • Reported, not hypothesised: the plating-weighted cycle-2 stoichiometry sits 0.15 to 0.22 above the law's window top on three sets and 0.04 on NCA_Kim2011 (x<sub>w</sub> 0.94 against 0.72 on Ai2020, 0.62 against 0.47 on Chen2020, 0.61 against 0.46 on OKane2022, 0.44 against 0.40 on NCA_Kim2011), and the node x<sub>i</sub>(2) span 0.36 to 0.46 of the stoichiometry range through the thickness. The one-point variant (one reading at x<sub>w</sub>) gives 0.091, 0.027, 0.044, 0.024: better than A on both LG M50 sets and close to 5zl's diagnosis on Chen2020 (0.027 against 0.025), worse on Ai2020. N at 25.3 ρ<sub>node,10</sub> gives 0.068, 0.056, 0.039, 0.075. These were read after the verdicts and are not tests; no variant wins on all four sets.
  • Reading: 5zm's mechanism is right about the rise. On LG M50 and Ai2020 the plating sits well above the law's window top in stoichiometry (deeper in lithiation, off the plateau the window top reads), and the law's own lithium-to-stoichiometry shift read there reproduces the measured plating-weighted rise on Chen2020 from cycle 10 (3.25 against 2.88 mV, where the law reads 0.42) and to within 2% at cycle 99. So the 1.35 to 1.49 factor 5zl found on LG M50 is mostly a reading-point error, not a different plating physics. What it does not do is forecast better everywhere at 25.3: on OKane2022 the node lever over-reads the early rise (5.49 against 3.00 mV) and the forecast overshoots, and on NCA_Kim2011, where the law's lever already read the rise right, swapping it loses half the accuracy (its rise is the same at cycle 10, 44.3 against 44.6 mV, so the difference is in how the lever extrapolates to the cycle-99 loss, which is 30 L(10) away). The forecast error therefore has a second part outside the lever's level: its shape beyond the first ten cycles' range. For a design search the advice of 5zm stands (fit the law's line through 30 to 50 cycles at 25.3); the node lever is worth using on Ai2020-like cells (thick, plateau-free top of charge), where it cuts the ten-cycle error by a factor of 3.6 on 7 of 8 designs.
  • Next: test the lever's extrapolation directly (the node lever's predicted rise at cycle 99 against the measured, given only cycles up to 10), and whether the OKane2022 overshoot comes from the nodes nearest the collector, whose x<sub>i</sub>(2) is lowest.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zm; cycle-2 weights; end-of-charge node OCPs are a model internal; inverting U<sub>n</sub> on the LG M50 plateau is ill-conditioned; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/plateau/results.txt, summary.json, rows.json, plateau.svg; tests tests/test_plateau.py.

2026-11-17 · Milestone 5zn: does a plateau-aware lever, the law's own uniform stoichiometry shift read at each node's cycle-2 stoichiometry on the OCP curve, reproduce the plating-weighted rise from cycle 2 and fix the ten-cycle forecast at the physical exponent? (plan, written and committed before the new lever was computed on any design; H204 to H208 are this entry's)

  • Question: 5zm found the plating-weighted OCP rise outruns the law's lever early on LG M50 (25.3 × the pointwise ratio 148 at cycle 10 on Chen2020, 30 at cycle 99) and named the cause: the law reads dU at the top of its uniform-stoichiometry window, which sits on the graphite plateau, while the plating sits at other stoichiometries through the thickness. The next step it named is a lever that reads the plating-weighted stoichiometry on the OCP curve. If the law's mapping of lost lithium to a stoichiometry shift is right and only the reading point is wrong, such a lever needs only cycle 2's node state, so it is available to a ten-cycle forecast, unlike 5zl's κ<sub>w</sub>.
  • Method, fixed now (experiments/plateau/run.py, rows, report; stdlib, no new simulation; 5zk's 40 designs and 5zl's balance, η and tables unchanged): x<sub>i</sub>(2) = U<sub>n</sub><sup>−1</sup>(u<sub>i</sub>(2)), each negative-electrode node's end-of-charge OCP at cycle 2 inverted on the set's U<sub>n</sub> table (a running-minimum envelope, since the LG M50 tables have flat steps; linear interpolation). The law's uniform shift s(l) = x<sub>hi</sub>(n<sub>Li</sub> − l; v<sub>hi</sub> − η) − x<sub>hi</sub>(n<sub>Li</sub> − L<sub>2</sub>; v<sub>hi</sub> − η) (5zd's window top). The node lever dU<sub>node</sub>(l) = Σ w<sub>i</sub>(2) U<sub>n</sub>(x<sub>i</sub>(2) + s(l)) minus its value at l = 0, w the cycle-2 plating shares (5zk). D<sup>node</sup><sub>n</sub> = dU<sub>node</sub>(L<sub>n</sub>) − dU<sub>node</sub>(L<sub>2</sub>); ρ<sub>node,k</sub> = least-squares slope through the origin of 5zl's M<sub>w,n</sub> on D<sup>node</sup><sub>n</sub> over n = 3..k. Forecast N: 5zf's forecast (line through cycles 2..10, κ = 25.3) with 5zm's tables but du replaced by dU<sub>node</sub>; A is 5zm's A<sub>10</sub> (5zd's lever, 25.3, line through 2..10). Error |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|, set medians over 8, 12, 12, 8 designs.
  • Already seen: 5zl's κ<sub>w</sub> and its errors, 5zm's A errors, pointwise ratios and early exponents on these designs; the U<sub>n</sub> tables' shape (checked for monotonicity only). Not seen: any x<sub>i</sub>(2), dU<sub>node</sub>, ρ<sub>node</sub> or forecast N.
  • H204 (the uniform shift read at the nodes reproduces the measured rise): set median |ln ρ<sub>node,99</sub>| at most 0.15 on at least 3 of 4 sets. Refuted if above 0.3 on 3 or more. (5zl's law lever gives |ln(κ<sub>w</sub>/25.3)| of 0.40 and 0.30 on LG M50.)
  • H205 (and it does so early, where 5zm's ratio did not): set median |ln ρ<sub>node,10</sub>| at most 0.3 on at least 3 of 4 sets. Refuted if above 0.6 on 3 or more.
  • H206 (the honest ten-cycle forecast): N's set median error is below A's on at least 3 of 4 sets. Refuted if on at most 1.
  • H207 (design by design): N beats A on at least 26 of 40 designs (one-sided sign test p < 0.05). Refuted if on 20 or fewer.
  • H208 (it closes most of the gap to 5zl's diagnosis): on both LG M50 sets N's set median error is at most 1.5 × 5zl's error at κ<sub>w</sub> (0.025 Chen2020, 0.019 OKane2022). Refuted if above 3 × on both.
  • Reported, not hypothesised: a one-point variant (x<sub>w</sub>(2) = U<sub>n</sub><sup>−1</sup> of the plating-weighted cycle-2 OCP, one reading point instead of the node sum), ρ<sub>node,k</sub> at k = 20, 30, 50, the plating-weighted x<sub>i</sub>(2) against the window top, and N with κ = 25.3 ρ<sub>node,10</sub>.
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs), all seen in 5zk to 5zm; cycle-2 weights; end-of-charge node OCPs are a model internal, so a forecast that uses them asks what a ten-cycle DFN run can tell a design search, not what a lab test records; inverting U<sub>n</sub> on a plateau is ill-conditioned (a small OCP error moves x a lot, though the lever then reads the same flat region); the uniform shift assumes every node loses stoichiometry at the window top's rate; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zm outcome: the plating-weighted lever cannot be read early on LG M50. Cut at k cycles, its exponent is 100 (the clamp) on Chen2020 at 10, 20 and 30 cycles and 49 to 75 on OKane2022, against 38 and 34 at 99, because the plating-weighted OCP rise outruns the law's lever early and the ratio falls all the way to cycle 99 (pointwise, 25.3 × ratio is 148, 81, 58, 30 at cycles 10, 30, 50, 99 on Chen2020). On NCA_Kim2011 it is flat from cycle 10 (28.5 to 26.0), and on Ai2020 it settles by 30 cycles (24.0 against 25.2). A forecast at the early exponent loses to the physical 25.3 given the same cycles on 4 of 4 sets at 10 cycles and 3 of 4 at 30. H200 and H202 refuted, H201 and H203 inconclusive

  • Analysis: stdlib, 19 s (rows), report run once. Reproduces 5zl exactly (κ<sub>w,99</sub> and the 25.3 error with a ten-cycle line equal 5zl's committed values on all 40 designs, tested). No design fell back to 25.3 (D carried signal on all 40 at every budget). After the verdicts the rows step was rerun once to add one per-design field for the post hoc (κ from the pointwise cycle-99 ratio); the report's numbers did not change.
  • H200 refuted (0 of 4): at k = 10 the set median error of B (the law at κ<sub>w,10</sub>) against A (at 25.3) is 0.289 against 0.083 (Ai2020), 0.171 against 0.082 (Chen2020, where κ<sub>w,10</sub> is clamped at 100), 0.066 against 0.059 (OKane2022) and 0.041 against 0.022 (NCA_Kim2011).
  • H201 inconclusive (2 at most 0.15, 2 above 0.3): set median |ln(κ<sub>w,30</sub>/κ<sub>w,99</sub>)| is 0.067 (Ai2020), 0.681 (Chen2020), 0.728 (OKane2022), 0.037 (NCA_Kim2011).
  • H202 refuted (1 of 4): at k = 30, B against A is 0.034 against 0.039 on Ai2020 (the one win), 0.133 against 0.046, 0.152 against 0.028 and 0.019 against 0.013.
  • H203 inconclusive: within-set Spearman(κ<sub>w,30</sub>, κ) is 0.83 (Ai2020), 0.23 (Chen2020), 0.87 (OKane2022), −0.24 (NCA_Kim2011, whose κ spans only 18.5 to 28.9, as 5zl).
  • Not hypothesised, in the table: the physical-exponent forecast with its line fitted through more cycles improves steadily on every set (A at k = 10, 30, 50: Chen2020 0.082, 0.046, 0.020; OKane2022 0.059, 0.028, 0.017; Ai2020 0.083, 0.039, 0.032; NCA_Kim2011 0.022, 0.013, 0.011). Keeping the ten-cycle line and only the early exponent (C) is no better than B.
  • Post hoc (run.py posthoc, posthoc.txt, after the verdicts): 25.3 × the pointwise ratio (plating-weighted rise) / (law's rise) from cycle 2 to k, set medians at k = 10, 20, 30, 50, 99: Chen2020 148, 111, 81, 58, 30; OKane2022 63, 79, 79, 51, 29; Ai2020 52, 27, 21, 23, 29; NCA_Kim2011 28.5, 27.4, 27.0, 26.5, 26.0. B beats A on 3, 4, 4, 3 of 12 Chen2020 designs at the four budgets.
  • Reading: on LG M50 the ratio 5zl found is not a constant of the design that early cycles reveal. In the first tens of cycles the OCP where the plating sits rises several times faster than the law's uniform-stoichiometry lever (whose window sits on the graphite plateau, 0.4 mV of rise by cycle 10 on Chen2020 against 2.9 mV plating-weighted), and the two converge only as lost lithium pushes the law's window off the plateau. So 5zl's κ<sub>w</sub> is a path average dominated by late cycles, and the forecast law's missing piece on LG M50 is the shape of its lever near the plateau, not one exponent. On NCA_Kim2011 (no plateau at the top of charge) the exponent is the physical one to within 10% from cycle 10. For a design search the practical answer is the plain one: run the DFN 30 to 50 cycles and fit the law's line at 25.3; that halves to quarters the ten-cycle error on every set, and no early exponent beats it on LG M50. The next mechanism step is a lever that reads the plating-weighted stoichiometry on the OCP curve (a plateau-aware dU), tested against the pointwise ratio's decay above.
  • Caveats: one pool per set (8, 12, 12, 8 designs), all seen in 5zk and 5zl; cycle-2 weights; end-of-charge node OCPs are a model internal; the A-versus-B comparison gives both the same cycles, but A at k > 10 is not the programme's ten-cycle forecast; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/horizon10/results.txt, summary.json, posthoc.txt, rows.json, horizon.svg; tests tests/test_horizon10.py.

2026-11-17 · Milestone 5zm: how many cycles does the plating-weighted lever need before it sets the plating exponent? A horizon test on 5zk's x-resolved records, with every forecast given the same cycles as its exponent (plan, written and committed before any early-window ratio or forecast was computed; H200 to H203 are this entry's)

  • Question: 5zl found that 25.3 × (plating-weighted end-of-charge OCP rise) / (the law's lever rise), fitted over cycles 3..99, lands within 3 to 12% of the oracle κ* on three of four sets. That reads cycle 99, so it is a diagnosis. 5zi's H186 found the separator-node lever unreadable in ten cycles on LG M50 (0.0 mV of rise on Chen2020 by cycle 10). The practical question is how early the plating-weighted lever settles: if it can be read by cycle 20 or 30, a design search can stop its DFN runs there and forecast cycle 99 with a per-design exponent instead of 5zh's 80 earlier 100-cycle runs per set.
  • Method, fixed now (experiments/horizon10/run.py, rows, report; stdlib, no new simulation): per design on 5zk's 40 designs, 5zl's η, κ* and tables unchanged (wlever _row inputs). For a budget of k cycles, k ∈ {10, 20, 30, 50}: κ<sub>w,k</sub> = 25.3 × the least-squares slope through the origin of M<sub>w,n</sub> on D<sub>n</sub> over n = 3..k (5zl's quantities, cut at k), clamped to [0, 100]; when D carries no signal (5zi's ratio returns None) the exponent falls back to 25.3 (count reported). Two forecasts of L(99) with the same budget: A<sub>k</sub> = the law at 25.3 with its line fitted through cycles 2..k; B<sub>k</sub> = the law at κ<sub>w,k</sub> with its line fitted through cycles 2..k (5zf's forecast with k). Error |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|, set medians over 8, 12, 12, 8 designs. κ<sub>w,99</sub> is 5zl's κ<sub>w</sub>.
  • Already seen: 5zl's κ<sub>w</sub>, κ* and errors at 25.3 and κ<sub>w</sub> (line through 2..10) on these designs; 5zi's ten-cycle separator-node result on other pools. Not seen: any M<sub>w</sub> or D cut before cycle 99, any forecast with a line through more than ten cycles.
  • H200 (ten cycles are enough, the honest forecast): at k = 10 the set median error of B is below A's on at least 3 of 4 sets. Refuted if on at most 1. (Expected to be hard on LG M50, after 5zi's H186.)
  • H201 (the lever settles by 30 cycles): the set median |ln(κ<sub>w,30</sub>/κ<sub>w,99</sub>)| is at most 0.15 on at least 3 of 4 sets. Refuted if above 0.3 on 3 or more.
  • H202 (an early read pays): at k = 30 the set median error of B is below A's on at least 3 of 4 sets. Refuted if on at most 1.
  • H203 (it still ranks designs): within-set Spearman(κ<sub>w,30</sub>, κ*) at least 0.4 on at least 3 of 4 sets. Refuted if under 0.15 on 3 or more.
  • Reported, not hypothesised: the same at k = 20 and 50, the fallback counts, and B with the line through cycles 2..10 only (exponent from k cycles, the law's ten-cycle fit unchanged).
  • Caveats fixed now: one pool per set (8, 12, 12, 8 designs, 5z's picks), all seen in 5zk/5zl; cycle-2 weights; end-of-charge node OCPs are a model internal, not a cell measurement, so this asks how long a DFN run must be, not what a lab test must record; κ* reads cycle 99 by construction; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zl outcome: read on the same designs, the plating-weighted OCP lever does set the plating exponent. On 5z's 40 designs, 25.3 times (plating-weighted end-of-charge OCP rise) / (the law's lever rise) lands within 3 to 12% of the oracle κ* on LG M50 and NCA_Kim2011 (set medians 37.7 against 36.6, 34.2 against 32.3, 26.4 against 23.6) and 34% high on Ai2020 (25.2 against 18.8, where the separator node gives 43.6). It is closer to κ* than the separator-node reading on 37 of 40 designs (sign test p = 10<sup>−8</sup>) and ranks designs within a set (Spearman 0.83 to 0.95 on three sets). 5zk's refutation came from comparing pools at other currents. H198 and H199 supported, H195 to H197 inconclusive

  • Analysis: stdlib, 14 s (rows), report run once, nothing in experiments/wlever/run.py changed after the plan apart from adding the post hoc command after the verdicts. All 40 designs gave κ* and both levers; 3 LG M50 designs have κ<sub>sep</sub> = 0 (the separator node's OCP does not rise past cycle 2), and none has κ<sub>w</sub> = 0.
  • H195 inconclusive: set median κ<sub>sep</sub> here against 5zi's κ<sub>path</sub> is 43.6 against 73.5 on Ai2020 (41% off), 40.5 against 33.0, 37.5 against 36.6 and 17.3 against 22.6. 5z's Ai2020 pool runs at 0.45 C-multiple; 5zi's six Ai2020 pools at 0.525 to 0.65, whose separator-node rise is 102 to 136 mV against 72 mV here, while the law's lever rises about the same (41 to 43 mV, 41 here).
  • H196 inconclusive: set median κ* is 18.8 (5zi 20.8), 36.6 (52.3, 30% off), 32.3 (38.1) and 23.6 (23.0). Chen2020's κ* spreads widely within the pool (9.7 to 75.6).
  • So 5zk's H193 compared a depth ratio from one pool with κ<sub>path</sub> and κ* from pools at other currents, and both sides of that comparison moved. Its "refuted" stands as stated but its reading (the set differences sit in the law's lever, not the measured one) does not survive the same-design test.
  • H197 inconclusive (4 of 4 sets closer, Ai2020 misses the 25% line): set median |ln(κ<sub>w</sub>/κ)| 0.307, 0.148, 0.119, 0.056 against the separator node's 0.839, 0.531, 0.439, 0.252. Ai2020's set median κ<sub>w</sub> is 34% above its κ; two of its eight designs (j 15 and 31, κ<sub>w</sub> 36 and 68 against 24 and 29) carry most of that.
  • H198 supported: within-set Spearman(κ<sub>w</sub>, κ) is 0.95 (Ai2020), 0.83 (Chen2020), 0.94 (OKane2022) and −0.17 (NCA_Kim2011, where κ spans only 18.5 to 28.9). The separator node gives 0.93, 0.38, 0.40, 0.90.
  • H199 supported (3 of 4; a diagnosis, the lever reads cycle 99): set median forecast error |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))| at κ<sub>w</sub> is 0.025 on Chen2020 (0.082 at 25.3), 0.019 on OKane2022 (0.059) and 0.012 on NCA_Kim2011 (0.022); on Ai2020 0.085 against 0.083. At κ<sub>sep</sub> it is worse than 25.3 on every set (0.261, 0.101, 0.084, 0.048).
  • Post hoc (run.py posthoc, posthoc.txt, after the verdicts): κ<sub>w</sub> is closer to κ* than κ<sub>sep</sub> on 8/8, 11/12, 11/12 and 7/8 designs (37 of 40, one-sided sign test p = 10<sup>−8</sup>); the forecast at κ<sub>w</sub> beats 25.3 on 28 of 40 (p = 0.008; 11 of 12 on Chen2020, 4 of 8 on Ai2020 and NCA_Kim2011) and beats κ<sub>sep</sub> on 36 of 40.
  • Reading: the plating exponent the law needs is, to within 3 to 12% on three of four cells, the physical αF/RT scaled by how much faster the OCP rises where the plating is than the law's uniform-stoichiometry lever. On LG M50 the law's lever under-reads that rise by a factor of 1.35 to 1.49 (the forecast needs 1.28 to 1.44); on NCA_Kim2011 it reads it right. So κ* is a measured quantity, as 5zi hoped, but measured through the thickness, not at the separator node. It still needs cycle 99's OCPs: the next question is whether the plating-weighted rise can be forecast from ten cycles or from the open-circuit balance, and why Ai2020 (the one cell modelled with 34 parallel electrode pairs) stays a third high.
  • Caveats: one pool per set (8, 12, 12, 8 designs) at one current per set; seen data (cycle 99 is in both the lever and κ*); cycle-2 weights; end-of-charge OCPs; the charge Ah from the constant-current charge time; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/wlever/results.txt, summary.json, posthoc.txt, rows.json, wlever.svg; tests tests/test_wlever.py.

2026-11-17 · Milestone 5zl: on the same designs, is the plating exponent the forecast needs 25.3 times the ratio of the plating-weighted OCP rise to the law's lever rise? A per-design test on 5zk's x-resolved records, which carry everything the law needs (plan, written and committed before any ratio or κ* on these designs was computed; H195 to H199 are this entry's)

  • Question: 5zk read the lever where the plating is and found it does not set κ, but the comparison was across pools: the measured depth ratio came from 5z's 40 designs, κ<sub>path</sub> and κ from 5zi's 768 others. Its reading put the remaining set differences on the law's side of the ratio and named the next step: compare the law's lever dU<sub>η</sub>(L<sub>n</sub>) with the plating-weighted measured OCP rise, per cycle, on 5z's designs. 5zk's records hold the lost lithium per cycle and the constant-current charge time (so the charge Ah is I t<sub>ch</sub>/3600, the experiment has no voltage hold), which is all 5zd's η and 5zf's oracle need. So κ*, the law's lever and both measured levers can be computed on the same 40 designs, with no new simulation.
  • Method, fixed now (experiments/wlever/run.py, rows, report): per design, 5zd's η from cycles 2..10 and 5zc's du_eta unchanged (balance from the pool 5z drew the design from: crossset, calmap for Ai2020); D<sub>n</sub> = dU<sub>η</sub>(L<sub>n</sub>) − dU<sub>η</sub>(L<sub>2</sub>); M<sub>sep,n</sub> = u<sub>sep</sub>(n) − u<sub>sep</sub>(2) (5zi's lever); M<sub>w,n</sub> = Σ w<sub>i</sub>(2)(u<sub>i</sub>(n) − u<sub>i</sub>(2)) (5zk's M<sub>w</sub>, now at every cycle); ρ = least-squares slope through the origin over n = 3..99 and κ = 25.3ρ clamped to [0, 100], as 5zi; κ* = 5zf's oracle; forecast errors |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))| at 25.3, κ<sub>sep</sub>, κ<sub>w</sub> and κ*. Set medians over 8 (Ai2020), 12, 12 and 8 designs.
  • Already seen: 5zk's set medians of M<sub>sep</sub> and M<sub>w</sub> at cycle 99 and their ratio (0.64, 0.81, 0.78, 1.21); 5zi's set medians of κ<sub>path</sub> and κ* on other pools. Not seen: η, D<sub>n</sub>, κ* or any κ on these designs.
  • H195 (5zi's separator lever transfers to 5z's pool): the set median κ<sub>sep</sub> is within 25% of 5zi's set median κ<sub>path</sub> (73.5, 33.0, 36.6, 22.6) on all four sets. Refuted if more than 50% off on any.
  • H196 (so does κ): the set median κ is within 25% of 5zi's (20.8, 52.3, 38.1, 23.0) on all four sets. Refuted if more than 50% off on any. (If H195 or H196 fails, 5zk's cross-pool H193 rested on a mismatch.)
  • H197 (the plating-weighted lever explains κ* better, design by design): the set median of |ln(κ<sub>w</sub>/κ)| is below that of |ln(κ<sub>sep</sub>/κ)| on at least 3 of 4 sets, and Ai2020's set median κ<sub>w</sub> is within 25% of its set median κ*. Refuted if below on at most 1 set.
  • H198 (it ranks designs): the within-set Spearman(κ<sub>w</sub>, κ*) is at least 0.4 on at least 3 of 4 sets. Refuted if under 0.15 on 3 or more.
  • H199 (as a correction it helps the forecast, a diagnosis since it reads cycle 99): the set median forecast error at κ<sub>w</sub> is below the one at 25.3 on at least 3 of 4 sets. Refuted if on at most 1.
  • Caveats fixed now: one pool per set (7 to 12 designs, 5z's picks); the slope through the origin weights late cycles; cycle-2 weights for M<sub>w</sub>; end-of-charge OCPs, not the time profile; the charge Ah from the charge time at constant current (checked in a test, not against a recorded Ah, which these runs did not keep); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zk outcome: the plating is spread through the negative electrode (the separator node carries 8 to 19% of it at cycle 2, the plating-weighted depth is 0.53 to 0.72 of the thickness), and that spread explains 5z's NCA_Kim2011 index miss (the separator node's slowdown misses the electrode's by 0.28 in log there, 0.015 on LG M50). It does not explain the plating exponent: read where the plating is, the lever shrinks to 0.64 of the separator node's on Ai2020 and 0.78 to 0.81 on LG M50, so the implied exponent moves from 73 to 47 on Ai2020 (κ* 21) and further from κ* on Chen2020 (27 against 52) and OKane2022 (28 against 38). H191, H192 and H194 supported; H193 refuted

  • Bench: 40 DFN runs to cycle 100, about 6 minutes on 3 workers; Ai2020 design 7 was killed for memory (exit −9) with 3 workers and finished on a single-worker retry, so Ai2020 has 8 designs (5z had 7). Report run once on the 40; one change after it, before any reading: the committed bench.jsonl was rounded to 7 significant digits to halve its size (8.3 to 4.7 MB); re-running the report on it moved no printed number past the fourth digit (worst booked-plating reproduction 0 to 2.6 × 10<sup>−7</sup>).
  • H194 supported: on all 39 designs 5z also ran, the cycle-99 booked plating reproduces to 2.6 × 10<sup>−7</sup> relative, the separator-node end-of-charge OCP to under 0.0001 mV, and the log change of plating from the integrated node currents matches 5z's booked per-cycle log change within 0.0014. The 20-node mesh is uniform (widths equal to 2 × 10<sup>−15</sup>).
  • H191 supported: set-median separator-node share of cycle 2's plating Ai2020 0.124, Chen2020 0.194, OKane2022 0.194, NCA_Kim2011 0.076. The median node share rises steadily toward the separator on Ai2020 and LG M50 (collector node 0.016 to 0.032), and is nearly flat on NCA_Kim2011 (0.047 at the collector, 0.045 mid-electrode, 0.076 at the separator) (depth.svg); on every set most of the plating is inside the electrode: the plating-weighted depth is 0.62 (Ai2020), 0.72 (both LG M50) and 0.53 (NCA_Kim2011) of the thickness from the collector.
  • H192 supported: set median |Δ<sub>sep</sub> − Δ<sub>tot</sub>| is 0.282 on NCA_Kim2011 (total −4.42, separator node −3.95), 0.015 and 0.014 on LG M50, 0.053 on Ai2020. On NCA_Kim2011 the plating moves toward the separator over the 100 cycles (separator share 0.076 to 0.141, depth 0.53 to 0.63) because the inner nodes slow faster, so more than half of 5z's 0.49 index miss there is location; the rest is the index's end-of-charge form (medians, so the split is approximate).
  • H193 refuted: depth ratios (median M<sub>w</sub> / median M<sub>sep</sub>) are 0.644 (Ai2020; refutation line 0.425), 0.813 (Chen2020), 0.777 (OKane2022) and 1.207 (NCA_Kim2011), giving κ<sub>w</sub> 47.3, 26.8, 28.4 and 27.3 against κ* 20.8, 52.3, 38.1 and 23.0: within 25% on NCA_Kim2011 only. Cycle-99 weights give the same picture (0.637, 0.760, 0.730, 1.183).
  • Reading: what each set would need from a depth correction is a factor of 0.28 on Ai2020, 1.58 on Chen2020, 1.04 on OKane2022 and 1.02 on NCA_Kim2011. Reading the lever where the plating is gives 0.64, 0.81, 0.78 and 1.21: the right direction on Ai2020 only, too weak there, and wrong on Chen2020. Together with 5zj (the separator node's other terms give a similar 0.59 on Ai2020 and 0.80 on LG M50), two independent corrections of the lever's location and terms move the sets the same way, so the set differences in κ* are not in where or how the plating potential is read. They are in the other side of the ratio: the law's own lever dU<sub>η</sub>(L), its uniform-stoichiometry window, and how it maps lost lithium to a potential on each set's OCP curve. That is the next step: compare the law's dU<sub>η</sub>(L<sub>n</sub>) against the plating-weighted measured OCP rise per cycle on 5z's designs (both are now recorded), which needs no new simulation.
  • Caveats: one pool per set (7 to 12 designs, 5z's picks); κ<sub>path</sub> and κ* are set medians from other pools (5zb to 5zg), so H193 is a set-level comparison, as 5zj's; the weighted rise uses end-of-charge OCPs, not the time profile; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); 20 nodes in the negative electrode (5zj's doubled mesh moved the particle loss by 0.1%, not checked here for the profile); modelled fade only.
  • Output: experiments/depth/bench.jsonl (per node and cycle: plating over the cycle and over the charge, end-of-charge OCP, surface potential difference and plating overpotential), results.txt, summary.json, depth.svg; tests tests/test_depth.py.

2026-11-17 · Milestone 5zk: where through the negative electrode does the plating happen, and does reading the lever there give the exponent the forecast needs? x-resolved plating currents on 5z's re-run designs over 100 cycles (plan, written and committed before the bench; H191 to H194 are this entry's)

  • Question: 5zi found that the separator-surface OCP lever explains the plating exponent κ* on OKane2022 and NCA_Kim2011 but overshoots on Ai2020 (lever-implied 73 against κ* 21) and undershoots on Chen2020 (33 against 52); 5zj found that the separator node's other terms halve the Ai2020 overshoot and push the other sets further off. Every lever so far is read at one node, the separator side of the negative electrode. If the plating is spread through the thickness, the potential that slows it is the plating-weighted one, not the separator node's, and the set differences may be where the plating sits.
  • Bench, fixed now (experiments/depth/run.py): 5z's 40 designs (random.Random(18) picks from crossset Chen2020@1.5x 12, OKane2022@1.5x 12, NCA_Kim2011@0.875x 8 and calmap Ai2020@0.45x 8; 5z lost Ai2020 design 7 to a solver failure), DFN with SEI (solvent-diffusion limited) + irreversible plating to cycle 100, PyBaMM defaults (20 nodes in the negative electrode), one fresh process per run. Recorded per cycle and per negative-electrode node: the plating current integrated over the whole cycle, P<sub>i</sub>(n) = −∫ j<sub>pl,i</sub> dt; and at end of charge the OCP u<sub>i</sub>, the surface potential difference and the plating reaction overpotential. Also the booked plating and lithium-loss totals and the node positions.
  • Quantities (cycles 2 and 99, 1-based, as 5z): w<sub>i</sub>(n) = P<sub>i</sub>(n) / ΣP (the mesh is uniform in x; node widths are checked from the recorded positions); the separator-node share s(n) = w<sub>last</sub>(n); Δ<sub>tot</sub> = ln(ΣP(99) / ΣP(2)); Δ<sub>sep</sub> = ln(P<sub>last</sub>(99) / P<sub>last</sub>(2)); M<sub>sep</sub> = u<sub>last</sub>(99) − u<sub>last</sub>(2); M<sub>w</sub> = Σ w<sub>i</sub>(2) (u<sub>i</sub>(99) − u<sub>i</sub>(2)), the OCP rise where the plating was at cycle 2. The set's depth ratio is median(M<sub>w</sub>) / median(M<sub>sep</sub>) over its designs (a ratio of medians, because M<sub>sep</sub> is near zero on some LG M50 designs, 5zj), and the depth-read exponent is κ<sub>w</sub> = 5zi's set-median κ<sub>path</sub> × that ratio (Ai2020 73.5, Chen2020 33.0, OKane2022 36.6, NCA_Kim2011 22.6), against 5zi's set-median κ* (20.8, 52.3, 38.1, 23.0).
  • Already seen: 5z's separator-node records on these designs (its rate index misses the per-cycle plating change by a median 0.49 in log on NCA_Kim2011, 0.069 on Ai2020, 0.015 on LG M50), 5zi's κ<sub>path</sub> and κ*, 5zj's terms. Not seen: anything resolved in x.
  • H191 (the plating is spread): at cycle 2 the separator node carries under half of the electrode's plating (set median of s(2)) on all four sets. Refuted if over 0.8 on any.
  • H192 (location explains 5z's NCA_Kim2011 miss): the set median of |Δ<sub>sep</sub> − Δ<sub>tot</sub>| is at least 0.2 on NCA_Kim2011 and at most 0.1 on both LG M50 sets. Refuted if it is under 0.1 on NCA_Kim2011 (then the miss is the index's end-of-charge form, not where the plating is).
  • H193 (the lever read where the plating is): κ<sub>w</sub> within 25% of κ* on at least 3 of the 4 sets, Ai2020 among them. Refuted if Ai2020's κ<sub>w</sub> stays above 1.5 κ* (31.3), i.e. a depth ratio above 0.425 there.
  • H194 (the re-runs are 5z's runs): on every design the cycle-99 booked plating and the separator-node end-of-charge OCP reproduce 5z's records within 0.1% and 0.1 mV, and Δ<sub>tot</sub> from the integrated node currents matches the log change of 5z's booked per-cycle plating within 0.02. Refuted if any design misses by 10 times those.
  • Caveats fixed now: one pool per set, 7 to 12 designs; the 5zi κ<sub>path</sub> and κ* come from other pools (5zb to 5zg) than these designs (5z's), so H193 compares set-level quantities, as 5zj's terms did; cycle-2 weights for M<sub>w</sub> (the plating moves over 100 cycles; the cycle-99 weighting is reported, not hypothesised); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zj outcome: Ai2020's "unbooked" lithium loss is plating, as 5p and 5za had already shown. This plan missed that and re-asked a closed question; the ledger replicates it by a second route (the side currents, integrated directly, pass the lithium that leaves the particles to 0.01%), and a doubled mesh moves it by 0.1%. The question 5zi actually left open, which separator-node terms give back Ai2020's steep surface-OCP lever, has a partial answer from 5z's committed records: the intercalation overpotential and the shape of the charge profile give back about 41% of it (about 20% on LG M50), which halves the Ai2020 overshoot (lever-implied exponent 73 to 43 against κ* 21) and moves LG M50 further off. The separator node does not set κ*. H187, H189 and H190 supported; H188 refuted

  • Planning error, stated first: the plan said the gap's source was unseen and needed naming. It had been named in 5p (experiments/attribution/UPSTREAM.md: PyBaMM 26.10.1.1 books SEI and plating per electrode pair, L_y L_z, but totals lithium over A_cc = L_y L_z n_parallel, and Ai2020 has 34 electrodes in parallel), and 5za's outcome confirmed it on 128 runs and corrected 5z. The plan was written from the newest entries and the README's next step without searching the log for "parallel". So H187 and H188 re-test a known result. They are logged as replications, not findings.
  • Bench: 32 ten-cycle DFN runs, 3 workers, about 2 minutes; then 2 refined runs, which the plan fixed at x 40/40/40, r 60/60 with rtol = atol = 10<sup>−8</sup> over ten cycles. Those were killed for memory (exit −9) twice with 3 workers and once with 1. A doubled mesh (x and r all 40) at 10 cycles and 10<sup>−8</sup> was killed too. Deviation, made before any refined number was read: the refined runs use the doubled mesh, default tolerances and 3 cycles, compared against the base runs at cycle 3. The report was run once on the 30 base runs and once more with the two refined runs added; nothing else in run.py report changed.
  • H187 supported (a replication): on all eight Ai2020@0.45x designs the charge the negative side reactions pass, ∫ −a j L<sub>n</sub> A<sub>cc</sub> dt / F from PyBaMM's own volumetric currents, equals the lithium lost from the particles to 0.01% (median 18.26 mmol by cycle 10). The booked side-reaction loss is 1/34.000 of it (0.537 mmol) on every design. Lost from the electrolyte: 0.000.
  • H188 refuted (a replication of 5p): SEI alone loses 0.048 mmol in ten cycles against 18.26 with both reactions. Plating alone loses 18.29. On Ai2020 the loss is plating.
  • H189 supported: the doubled mesh changes the cycle-3 particle loss by 0.11% and 0.07% (designs 7 and 12). The base run of design 7 reproduces 5za's recorded 0.0053285 mol to the last digit.
  • H190 supported: on the six control designs (Chen2020, OKane2022, NCA_Kim2011, one electrode pair each) booked and lost agree to under 0.01%.
  • Post hoc, the question 5zi left (run.py terms, stdlib, on 5z's committed per-design records; their pool medians were seen before this step): 5z split the cycle-2-to-99 change of the separator-node plating exponent into terms. As shares of the surface-OCP term, the intercalation overpotential gives back 0.21 on Ai2020 (0.20 and 0.24 on LG M50, −0.01 on NCA_Kim2011). The charge-profile shape (the time-integrated rate index minus the end-of-charge terms and the charge time) gives back 0.23 on Ai2020 (range 0.18 to 0.36, all seven designs) against 0.02 and 0.04 on LG M50, and it adds 0.22 on NCA_Kim2011. So what is left of the OCP lever is 0.59 on Ai2020, 0.82 and 0.80 on LG M50 and 1.19 on NCA_Kim2011. Rescaling 5zi's set-median lever-implied exponent by that ratio gives Ai2020 43 (from 73; κ* 21), Chen2020 27 (from 33; κ* 52), OKane2022 29 (from 37; κ* 38) and NCA_Kim2011 27 (from 23; κ* 23). Every set but Ai2020 moves away from its κ*.
  • Reading: Ai2020 is a plating cell like the others, and everything fitted on it from 5u on fits plating on a consistent scale (balance.jsonl's n<sub>Li</sub> = 0.2520 mol equals PyBaMM's A<sub>cc</sub>-scaled particle total for design 7). Its odd exponent has a partial physical reason: on Ai2020 the plating spreads over more of the charge, so the end-of-charge node over-reads its slowdown, and the intercalation overpotential grows. Neither is enough, and on the other sets the same correction hurts. So κ* is not a property of the separator node. The next mechanism step is a through-thickness one: integrate PyBaMM's plating current over x and the charge (as this milestone's ledger already does for the total) and split its cycle-2-to-99 change by node, on 5z's re-run designs. If the spread in x carries the set differences, the lever should be read where the plating is, not at the separator.
  • Caveats: ten cycles for the ledger (the bookkeeping factor is structural and exact, so the horizon does not matter for H187); 3 cycles and default tolerances for the mesh check; the post hoc terms come from 5z's four pools (other pools than 5zi's 24) and compare cycles 2 and 99, not 5zi's slope over 3 to 99; shares are unstable on LG M50 designs whose OCP term is near zero (medians are shown, ranges in terms.txt); one PyBaMM version (26.10.1.1).
  • Output: experiments/ledger/bench.jsonl, results.txt, summary.json, terms.txt, terms.json; tests tests/test_ledger.py.

2026-11-17 · Milestone 5zj: where does Ai2020's unbooked lithium loss go? A lithium ledger of PyBaMM's DFN over ten cycles on 5z's designs, set against the charge the side reactions actually pass (plan, written and committed before the bench; H187 to H190 are this entry's)

  • Question: 5z found that on Ai2020@0.45x only 2.9% of PyBaMM's "Total lithium lost [mol]" at cycle 99 is booked to plating and 0.0% to SEI, while on the other three sets the booked side reactions are 98.7 to 100% of it; a 3-cycle check on one design saw 0.0053 mol leave the particles against 0.00016 mol booked, and nothing lost with SEI and plating both off. 5zi then found Ai2020 the one set the separator-surface lever cannot explain. Every Ai2020 result from 5u on fits this unbooked quantity, so its physics has to be named before Ai2020 counts as a second cell.
  • Bench, fixed now (experiments/ledger/run.py): DFN to cycle 10, one fresh process per run, at 5z's designs: all eight Ai2020@0.45x picks (random.Random(18), as 5z) in three variants (both = SEI solvent-diffusion limited + irreversible plating, as every 100-cycle milestone; sei only; plating only); the first two of them again with both on a doubled-or-more mesh (x 40/40/40, r 60/60 against the default 20s) and IDAKLU rtol = atol = 10<sup>−8</sup>; and the first two of 5z's picks on each control pool (Chen2020@1.5x, OKane2022@1.5x, NCA_Kim2011@0.875x), both. Recorded per cycle: every term of PyBaMM's lithium ledger (lithium in each electrode and the electrolyte; lost in total, from particles, from electrolyte, to side reactions; booked to SEI, SEI on cracks, plating, loss of active material in each electrode), and the charge the negative electrode's SEI, SEI-on-cracks and plating currents pass, ∫ −a j L<sub>n</sub> A dt / F from their x-averaged volumetric interfacial current densities (A the parallel electrode area).
  • Already seen: 5z's 100-cycle shares and its one 3-cycle check (above). [Added at the outcome: this was wrong. 5p and 5za had already explained the gap; see the outcome entry.] Not seen: any ledger term other than the totals, the passed charge, any single-reaction variant or any refined run.
  • H187 (the booking variables under-count): on every Ai2020 design (both) the passed side-reaction charge at cycle 10 is within 10% of the lithium lost from the particles. Refuted if it is within 10% of the booked side-reaction loss on at least half of them (then the side reactions really are small and the particles lose lithium another way).
  • H188 (SEI, not plating): in the sei variant the cycle-10 particle loss is at least 80% of the both variant's on every Ai2020 design. Refuted if under 50% on any.
  • H189 (not numerical): the refined runs change the cycle-10 particle loss by under 5% on both designs. Refuted if by over 20% on either.
  • H190 (Ai2020 only): on the six control designs the booked side-reaction loss is within 5% of the particle loss at cycle 10. Refuted if outside 20% on any.
  • Caveats fixed now: ten cycles, not 100 (the 3-cycle check says the gap is there from the start); eight Ai2020 designs from one pool; x-averaged currents (exact for the integral over x); OKane2022's SEI and plating parameters only where Ai2020 lacks its own (5p); one PyBaMM version (26.10.1.1). This milestone places the gap; if it is a bookkeeping or parameter inconsistency, naming the parameter is the step after.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zi outcome: the lever ratio explains the plating exponent the forecast needs on two of the four sets. On OKane2022 and NCA_Kim2011, 25.3 times (measured separator-surface OCP rise) / (the law's lever rise) lands within 25% of the oracle κ* on all 12 pools (ratio 0.80 to 1.13). On Chen2020 it explains half to nine-tenths of κ* (0.50 to 0.89), and on Ai2020 it is three times too high (2.75 to 3.77), so across the 24 pools it does not order κ* (Spearman −0.10). It cannot be read in ten cycles on LG M50, whose surface OCP has not moved by cycle 10 (0.0 mV on Chen2020). H185 supported, H184 and H186 refuted, H182 and H183 inconclusive

  • Analysis: 768 committed designs (24 pools), about 74 s for rows on 4 cores, report run once; nothing in experiments/lever/run.py changed after the plan. Every design gave a ρ<sub>path</sub> and a ρ<sub>10</sub>.
  • H182 inconclusive (7 of 12; supported at 10, refuted below 6): all six OKane2022 pools match (κ<sub>path</sub>/κ* 0.82 to 1.08), but only one Chen2020 pool does (0.89; the others 0.50 to 0.70). Pool medians: measured cycle-2-to-99 surface rise 30.8 to 39.4 mV on LG M50 against the law's 21.1 to 29.5 mV.
  • H183 inconclusive (6 of 12; supported at 8, refuted below 4): all six NCA_Kim2011 pools match (0.80 to 1.13; measured rise 107 to 146 mV against the law's 134 to 151 mV, so the lever is about right and so is 25.3). None of the six Ai2020 pools does: its surface OCP rises 102 to 136 mV while the law's lever rises 41 to 43 mV, which implies κ = 55 to 82 where the forecast needs 20 to 25.
  • H184 refuted: Spearman of pool κ<sub>path</sub> against pool κ* over the 24 pools is −0.095, because Ai2020 has the highest κ<sub>path</sub> and the lowest κ*.
  • H185 supported (just): the median within-pool Spearman(κ<sub>path</sub>, κ*) over the 12 LG M50 pools is 0.423 (OKane2022 0.33 to 0.72, Chen2020 0.03 to 0.46). Not hypothesised but in the table: within-pool ranks are strongest where the level is wrong, Ai2020 0.80 to 0.89, and 0.60 to 0.87 on NCA_Kim2011.
  • H186 refuted (0 of 12): over cycles 2 to 10 the LG M50 surface OCP rises 0.0 mV on every Chen2020 pool and 0.5 to 2.7 mV on OKane2022, so κ<sub>10</sub> is near 0 on Chen2020 (pool medians 0.0 to 0.2) and 3 to 27 on OKane2022, and the forecast at κ<sub>10</sub> errs by 0.136 to 0.270 against 25.3's 0.059 to 0.109.
  • Post hoc (after the verdicts, from the same table): the forecast at κ<sub>path</sub> beats 25.3 on 3 Chen2020, 2 OKane2022 and 4 NCA_Kim2011 pools and on no Ai2020 pool (0.235 to 0.319 against 0.056 to 0.081), and never beats 5zg's set calibration from 160 earlier runs. So even with cycle 99's own surface potential the lever ratio is a weaker forecast than one calibrated number per set.
  • Reading: where the law's lever under-reads the loaded separator-surface potential (OKane2022) or reads it about right (NCA_Kim2011), the exponent it needs is the physical one rescaled by that ratio, which is the mechanism 5zf proposed. Chen2020 is part of the way there: the ratio accounts for 50 to 89% of the steeper lever. Ai2020 breaks it completely: its surface OCP rises three times as fast as the law's lever, yet the forecast needs about the physical exponent, so on that set the OCP at the separator surface is not the potential that slows plating. The plating overpotential is φ<sub>s</sub> − φ<sub>e</sub>, not U, and 5za already saw that Ai2020 "predicts the surface rise exactly" while doing harm. The next mechanism step therefore needs pybamm: decompose the plating overpotential at the separator node (the surface OCP, the intercalation overpotential and the electrolyte potential) on re-run Ai2020 and Chen2020 designs, as 5z did on LG M50 at two cycles. A ten-cycle forecast cannot use this lever on LG M50, because the graphite surface sits on its plateau through cycle 10.
  • Caveats: seen data throughout; one node (the separator side); the slope through the origin weights late cycles; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/lever/results.txt, summary.json, lever.svg; rows.json (regenerated by rows) not committed; tests tests/test_lever.py.

2026-11-17 · Milestone 5zi: is the plating exponent the ten-cycle forecast needs the physical αF/RT scaled by how much faster the separator-surface potential rises than the law's lever? A test of the mechanism 5zf to 5zh left open, on the 768 committed designs (plan, written and committed before any ratio was computed; H182 to H186 are this entry's)

  • Question: 5zf to 5zh found that 5zd's law needs a per-set exponent (oracle κ* 30 to 57 V<sup>−1</sup> on LG M50, about 20 to 23 on the controls, against αF/RT = 25.3), and 5zh that calibrating it costs about 80 earlier long runs before it never loses to physics. The law reads the potential lever dU<sub>η</sub>(L), the rise of the negative OCP at the top of the η-shortened window. If the true lever that slows plating, the loaded separator-surface OCP u(n) the DFN records at end of charge (5z), rises ρ times as fast as dU<sub>η</sub>, the law's effective exponent is 25.3ρ. If that holds, κ* is a measured quantity, not a calibration.
  • Data: no new simulation. All 24 committed pools of 5zb to 5zg (32 designs each); every record carries u(n) for cycles 1 to 100 (checked: 768 of 768). Per design, with 5zd's η from cycles 2..10 and 5zc's du_eta unchanged: D<sub>n</sub> = dU<sub>η</sub>(L<sub>n</sub>) − dU<sub>η</sub>(L<sub>2</sub>), M<sub>n</sub> = u(n) − u(2); ρ<sub>path</sub> = the least-squares slope through the origin of M<sub>n</sub> on D<sub>n</sub> over n = 3..99 (a diagnosis: it uses cycle 99); ρ<sub>10</sub> = the same over n = 3..10 (a forecast); κ<sub>path</sub> = 25.3ρ<sub>path</sub>, κ<sub>10</sub> = 25.3ρ<sub>10</sub>, clamped to [0, 100]. κ* is 5zf's oracle (experiments/kappa/run.py), unchanged. Script experiments/lever/run.py (rows, report).
  • Already seen before this plan: κ* per pool (5zf to 5zh); 5zd's H161 pool medians of the measured cycle-99 surface rise (39 and 36 mV on its LG M50 pools, 118 mV on Ai2020) and of the η window's absolute error in forecasting it (21 and 17 mV; 75 mV on Ai2020), which hint that the law's lever is about half the measured one on LG M50 but do not give its sign or size on the controls; 5zf's law lever rise in ten cycles (under 1 mV on LG M50, 40 to 50 mV on NCA_Kim2011). Not seen: any ρ, per design or per pool.
  • H182 (the mechanism on LG M50): the pool median κ<sub>path</sub> within 25% of the pool median κ* on at least 10 of the 12 LG M50 pools. Refuted if on fewer than 6.
  • H183 (the mechanism on the controls): the same on at least 8 of the 12 Ai2020 and NCA_Kim2011 pools. Refuted if on fewer than 4.
  • H184 (it orders the sets): Spearman of pool median κ<sub>path</sub> against pool median κ* over the 24 pools at least 0.6. Refuted below 0.3.
  • H185 (it explains the within-set spread that 5zh found costly): the median over the 12 LG M50 pools of the within-pool Spearman(κ<sub>path</sub>, κ*) at least 0.4. Refuted below 0.15.
  • H186 (readable in ten cycles): the forecast at κ<sub>10</sub> has a lower pool median |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))| than at 25.3 on at least 9 of the 12 LG M50 pools. Refuted if on fewer than 6. (Expected to be hard: 5zf found the law's lever moves under 1 mV in ten cycles there.) The 5zg med calibration from the set's other 160 designs is reported alongside, not hypothesised.
  • Caveats fixed now: seen data throughout; ρ compares the separator-node OCP (one node) with a uniform-stoichiometry lever, so a match says the law's lever is mis-scaled, not why; the slope through the origin weights late cycles most; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Outcome to be logged above this entry.

2026-11-17 · Milestone 5zh outcome: ten earlier 100-cycle runs buy the per-set plating exponent's typical gain (every pool's median error within 0.007 of the 160-run calibration), but not its reliability: at ten runs the 90th-percentile pool still loses to the physical exponent on 10 of 24 pools (4 of 12 LG M50), and it takes about 80 runs before that tail is gone. One earlier campaign at another current is as good as scattered runs. H178 to H180 supported, H177 and H181 refuted

  • Analysis: 768 committed designs (24 pools), 500 resamples per cell, seed 5, about 6 s after the 1-minute rows step; the report was run once. One mechanical fix after the plan, before the report: the script registered its imported module in sys.modules so the worker pool could pickle the worker function (the first rows call failed on that, before any number was produced). Grid interpolation against the exact forecast at k = 160: largest pool gap 7 × 10<sup>−6</sup>.
  • H177 refuted: A, k = 10: the 90th percentile beats phys on 8 of 12 LG M50 pools. The four that miss are the pools where phys was already closest (kappa/OKane2022@1.40625x phys 0.059, q90 0.093; consistent/OKane2022@1.4375x 0.064 against 0.083; loaded/OKane2022@1.375x 0.071 against 0.083; loaded/Chen2020@1.375x 0.080 against 0.093). On the seven LG M50 pools where phys errs by more than 0.09, the k = 10 90th percentile is 0.061 to 0.086.
  • H178 supported: A, k = 10: the median over resamples is within +0.007 of the k = 160 error on every pool (largest gap consistent/OKane2022@1.4375x, 0.060 against 0.053). In the median, ten runs is the 160-run result.
  • H179 supported: A, k = 1: the 90th percentile is above phys on all 24 pools (worst 0.178, kappa/Ai2020@0.5875x). One design's oracle exponent is not a calibration.
  • H180 supported: B, k = 10 (ten designs from one earlier pool, one current) has its median within 0.01 of A, k = 10 on 24 of 24 pools; its 90th percentile is a little wider (worst 0.098 against 0.093). The current dependence 5zg found on LG M50 is too small, at these spacings, to bias a single-campaign calibration.
  • H181 refuted: no k below 160 brings every pool's 90th percentile within 0.01 of its k = 160 error (at k = 80 two Ai2020 pools stay out, consistent/Ai2020@0.575x 0.057 against 0.040 + 0.01 and loaded/Ai2020@0.525x 0.064 against 0.053 + 0.01; at k = 40 seven pools; 160 is trivially exact). Counting pools whose 90th percentile beats phys: 0 at k = 1, 5 at k = 3, 14 at k = 10, 18 at k = 20, 19 at k = 32, 21 at k = 80, 23 at k = 160.
  • Reading: the calibration's typical value settles fast (the median κ* of ten designs is close to the median of 160), so a search that can live with "usually better" needs about ten earlier long runs, from one campaign if that is what it has. What does not settle fast is the tail: κ's spread within a set (LG M50 interquartile about 30 to 65 V<sup>−1</sup>) makes a ten-run median land 13 to 16 V<sup>−1</sup> or more from the set's full median one time in ten (5.3 on Ai2020; 2000 draws from all six pools, seed 1, a check run after the report), and on the pools where the physical exponent was already within 6 to 8% that miss costs more than the calibration gains. Guaranteeing no loss against physics needs about 80 runs. The cheaper route to reliability is to shrink the spread, which is the mechanism question still open from 5zf: if κ/(αF/RT) is a quantity readable from the first ten cycles (the separator-surface rise against the open-circuit rise), it would replace the calibration's scatter with a per-design measurement.
  • Caveats: seen data throughout (20 of the 24 pools chose the med form in 5zg), so this measures the budget for a form already chosen; the earlier pools are at other currents of the same set, 32 designs each; the k-run draws are from the same Sobol bounds as the test pools; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/fewruns/results.txt, summary.json, fewruns.svg; rows.json (6.6 MB) is regenerated by rows and not committed; tests tests/test_fewruns.py.

2026-11-17 · Milestone 5zh: how many earlier 100-cycle DFN runs does 5zg's per-set plating exponent need? Resampling on the 768 committed designs (plan, written and committed before the resampling was run; H177 to H181 are this entry's)

  • Question: 5zg calibrated κ once per parameter set as the median oracle κ* over 160 earlier hundred-cycle DFN runs, which a design search would have to pay for before trusting its ten-cycle forecasts. Here 160 is the cost to cut: what does a budget of k earlier runs buy, and does it matter whether they come from one earlier campaign (one current) or are scattered across several?
  • Data: no new simulation. All 24 committed pools of 5zb to 5zg (32 designs each, six pools per set). Each pool is the test pool in turn, and its set's other five pools (160 designs) are the earlier runs. κ* and each design's error on 5zg's 0.25 V<sup>−1</sup> grid are computed by 5zg's unchanged design and errs_on_grid (experiments/fewruns/run.py rows); the pool score at a resampled κ is the median over the pool's designs of the linearly interpolated |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|, checked against the exact forecast at k = 160.
  • Two ways to spend k runs, each resampled 500 times (seed 5): A, k designs without replacement from all 160; B, one of the five earlier pools at random, then k of its 32 designs. k = 1, 2, 3, 5, 10, 20, 32 (both), 40, 80, 160 (A). κ = the median κ* of the k designs (5zg's med). For each cell: the median and the 90th percentile over resamples of the pool's error.
  • Already seen before this plan: the per-pool medians and quartiles of κ* (5zf, 5zg) and the med errors with 128 or 160 training designs; not seen: any error at k below 128 or from a single pool.
  • H177 (ten runs suffice where it matters): A, k = 10: the 90th percentile below the phys error (κ = 25.3) on all 12 LG M50 pools. Refuted if on fewer than 9.
  • H178 (ten runs nearly match 160): A, k = 10: the median within 0.01 of the k = 160 error on all 24 pools. Refuted if more than 0.02 above it on any pool.
  • H179 (one run is a gamble): A, k = 1: the 90th percentile above phys on at least 6 of the 24 pools. Refuted if on fewer than 3.
  • H180 (one campaign is as good as scattered runs): B, k = 10: the median within 0.01 of A, k = 10 on at least 20 of the 24 pools. Refuted if on fewer than 16. (5zg found LG M50's κ* falls with current, so one campaign at another current could carry a bias.)
  • H181 (the budget): the smallest k (A) at which every pool's 90th percentile is at most its k = 160 error + 0.01 is at most 20. Refuted if above 40 or never reached.
  • Caveats fixed now: the earlier pools are at other currents of the same set (no pool is calibrated on its own current); the test pools are all seen data, 20 of them already used to choose the med form in 5zg, so this measures the budget, not the form; one current per pool; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/fewruns/run.py; outcome to be logged above this entry.

2026-11-17 · Milestone 5zg outcome: one plating exponent per parameter set, calibrated on that set's earlier 100-cycle runs, removes the ten-cycle forecast's bias on all four fresh pools. LG M50's cycle-99 lithium-loss error falls from 9.3% and 7.6% to 4.9% and 6.5%, the controls improve too (Ai2020 5.6% to 4.9%, NCA_Kim2011 1.7% to 0.9%), and the worst pool goes from 0.093 to 0.065. H172 to H176 supported

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 25, 3 workers, about 20 minutes on 4 cores. Three runs (Ai2020@0.5375x designs 1, 6 and 19) were killed for memory (exit −9, not the solver) and re-run with one worker, as the plan fixed; none was dropped, so there are 32 designs per pool. The report was run once, after the bench. experiments/setkappa/run.py's dev, design, calibrate and the plan's calibration were not changed after the plan; report, verdicts and the figure were written while the bench ran, before any fresh result was read.
  • Median |ln(L(99)/L<sub>DFN</sub>(99))|, phys (25.3) against med (the set's median oracle κ*): Chen2020@1.265625x 0.093 to 0.049 (κ 49.7), OKane2022@1.28125x 0.076 to 0.065 (38.6), Ai2020@0.5375x 0.056 to 0.049 (21.0), NCA_Kim2011@0.65625x 0.017 to 0.009 (22.7). med beats phys on 23, 21, 18 and 21 of 32 designs. The signed median error goes from +0.091, +0.073, −0.048, −0.016 to +0.006, +0.018, +0.004, +0.004: the systematic over-prediction on LG M50 and under-prediction on the controls are gone. Spearman of the med forecast against the true loss is 0.959 and 0.966 on LG M50, 0.992 and 0.999 on the controls.
  • H172 supported (0.049 < 0.093, 0.065 < 0.076). H173 supported (0.049, 0.065 ≤ 0.07). H174 supported (controls improve). H175 supported (worst 0.065 against 0.093).
  • H176 supported: line (κ* a line in the C-rate) beats med on both LG M50 pools, 0.046 against 0.049 (Chen2020, κ 53.5) and 0.058 against 0.065 (OKane2022, κ 47.4); the fresh pools' own oracle medians were 51.7 and 43.3, so LG M50's exponent does fall with current. err (least pooled error) did as well here (0.043, 0.053) though it overfit OKane2022 in dev; it was not in a hypothesis.
  • Reading: the ten-cycle plating forecast is now inside 7% on all four fresh pools and its sign errors are gone, using the design's balance, its first ten cycles, and one number per parameter set from that set's earlier 100-cycle runs. On the controls the calibrated exponent is close to αF/RT (21 and 23 against 25.3), so it is a small correction there; on LG M50 it is 1.5 to 2 times larger, and it moves with current. That LG M50 needs a steeper effective lever is what the law cannot derive: the next step is the mechanism 5zf named (is the oracle ratio κ*/(αF/RT) the ratio of the separator-surface potential rise to the open-circuit rise the law reads?), which would replace the calibration with something read from ten cycles, and a cost check of how few earlier 100-cycle runs the calibration needs (here 160 per set; a design search would want fewer than 10).
  • Caveats: one current per set; the calibration used 160 earlier hundred-cycle runs per set; the form was chosen after a leave-one-pool-out dev on the same seen pools the calibration uses; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/setkappa/bench.jsonl, balance.jsonl, ocp.json, dev.txt, dev.json, results.txt, summary.json, setkappa.svg; tests tests/test_setkappa.py.

2026-11-16 · Milestone 5zg: does one plating exponent κ per parameter set, calibrated on that set's earlier 100-cycle DFN runs, fix the ten-cycle plating forecast on fresh designs at new currents? Leave-one-pool-out on the 640 committed designs, then a pre-registered fresh bench (plan, written before any fresh run; H172 to H176 are this entry's)

  • Question: 5zf showed κ cannot be read from a design's own ten cycles on LG M50, and that the oracle κ* sits at 30 to 57 V<sup>−1</sup> there against αF/RT = 25.3. A design search has earlier 100-cycle runs of the same parameter set to hand, so it can calibrate κ once per set and then forecast every new design from ten cycles. 5zd's law is unchanged (experiments/kappa/run.py: tab, forecast, kappa_oracle); only κ moves (experiments/setkappa/run.py).
  • Three calibrations per set, each from the set's training designs: med, the median oracle κ*; err, the κ on a 0.25 V<sup>−1</sup> grid with the least pooled median |ln(L<sub>pred</sub>(99)/L<sub>DFN</sub>(99))|; line, κ* a least-squares line in the C-rate multiplier, read at the target current. phys is 25.3.
  • Seen (dev; python experiments/setkappa/run.py dev, experiments/setkappa/dev.txt): leave one pool out over the 20 committed pools of 5zb to 5zf (640 designs, five pools per set), each pool forecast with κ calibrated on its set's other four pools. med beats phys on 19 of 20 pools, worst pool 0.078 against 0.109; LG M50 0.041 to 0.078 against 0.059 to 0.109; Ai2020 0.040 to 0.068 against 0.063 to 0.081 (worse on one pool, 0.067 against 0.065); NCA_Kim2011 0.008 to 0.016 against 0.018 to 0.029. line wins 18 of 20, worst 0.069; it beats med most at the low end of the LG M50 range (kinetic/OKane2022@1.25x 0.039 against 0.075), because LG M50's κ* falls with current (slopes −89 and −95 V<sup>−1</sup> per unit C-rate multiplier on Chen2020 and OKane2022). err wins 14 and overfits on OKane2022 (0.080 to 0.094 on three pools). med is the primary form because it is the simplest and won most pools; line is the secondary.
  • Calibration for the fresh bench, fixed now (all 160 seen designs per set): med 20.98 (Ai2020), 22.74 (NCA_Kim2011), 49.68 (Chen2020), 38.61 (OKane2022); line κ* = 10.0 + 23.3c, 18.5 + 7.2c, 165.5 − 88.5c, 169.4 − 95.3c.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 25, used by no milestone; energy-cell bounds) on each of Ai2020@0.5375x, NCA_Kim2011@0.65625x, Chen2020@1.265625x, OKane2022@1.28125x, currents no milestone has used, inside each set's dev range; the LG M50 currents sit at the low end, where med and line part most (line reads 53.5 and 47.3 V<sup>−1</sup> there). 128 DFN runs (SEI + plating) to cycle 100 with 5zc's simulate unchanged, 3 workers; memory kills retried with one worker; failed runs dropped and counted.
  • H172 (the per-set exponent helps LG M50): med's median |ln err| below phys's on both LG M50 pools. Refuted if on neither.
  • H173 (LG M50 inside 7%): med at most 0.07 on both LG M50 pools. Refuted above 0.10 on either.
  • H174 (controls not harmed): med at most phys + 0.01 on both control pools. Refuted if worse by more than 0.03 on either.
  • H175 (the worst pool improves): med's worst pool below phys's worst pool and at most 0.08. Refuted if med's worst pool is no better than phys's.
  • H176 (current matters on LG M50): line below med on both LG M50 pools. Refuted if above med on both.
  • Caveats fixed now: one current per set; calibration uses five earlier pools per set (160 hundred-cycle runs), which a real search would have to pay for; the form was chosen after the leave-one-pool-out dev; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only. The mechanism question 5zf also raised (whether LG M50's steeper lever is the ratio of the separator-surface rise to the open-circuit rise) is not tested here.
  • Script: experiments/setkappa/run.py; outcome to be logged above this entry.

2026-11-16 · Milestone 5zf outcome: the plating law's kinetic exponent cannot be read from a design's first ten cycles on LG M50, and fitting it per design makes the cycle-99 forecast worse on all four fresh pools. But the κ each set would need is not the same: LG M50 needs a steeper potential lever (median oracle κ* 45 and 32 V<sup>−1</sup>, against αF/RT = 25.3), while Ai2020 and NCA_Kim2011 need about the physical value (20 and 23). H167 to H171 supported

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 24, 3 workers, about 33 minutes on 4 cores. One run (Ai2020@0.5875x design 1) was killed for memory (exit −9, not the solver) and re-run with one worker, as the plan fixed; none was dropped, so there are 32 designs per pool. The report was run once, after the bench. experiments/kappa/run.py was not changed after the plan.
  • 5zd at κ = 25.3 replicates again: median |ln(L(99)/L<sub>DFN</sub>(99))| 0.099 (Chen2020@1.34375x) and 0.059 (OKane2022@1.40625x), 0.081 (Ai2020@0.5875x, signed −0.059), 0.019 (NCA_Kim2011@0.71875x). κ = 0 is 0.25 to 0.39.
  • H167 supported: the lever rises by 0.7 and 0.6 mV over cycles 2 to 10 on the LG M50 pools; the ten-cycle fit sits at the 100 V<sup>−1</sup> bound on 21 of 32 Chen2020 designs (median 100) and 13 of 32 OKane2022 designs (interquartile 15 to 98).
  • H168 supported: fit forecasts worse than κ = 25.3 on both controls (Ai2020 0.090 against 0.081, NCA_Kim2011 0.054 against 0.019), and on both LG M50 pools too (0.127 against 0.099, 0.122 against 0.059). slope is no better (0.092, 0.054, 0.127, 0.090).
  • H169 supported: median κ* 45.4 V<sup>−1</sup> (interquartile 29.7 to 65.4) on Chen2020 and 31.7 (23.9 to 47.7) on OKane2022.
  • H170 supported: median κ* 20.4 (17.3 to 33.3) on Ai2020 and 22.9 (22.2 to 25.9) on NCA_Kim2011.
  • H171 supported: Spearman(fit, κ*) 0.721 on NCA_Kim2011 (lever +46 mV in ten cycles), 0.083 and 0.589 on the LG M50 pools; Ai2020 (+6.5 mV) −0.126.
  • Reading: on all ten LG M50 pools now checked (eight seen, two fresh), the law with the physical κ over-predicts because, at a constant η, its potential lever is too shallow there: the oracle's pool medians are 30 to 57 V<sup>−1</sup>, 1.2 to 2.3 × αF/RT. On the two control sets the physical κ is about right, and Ai2020's error is design-to-design scatter in κ* around 20 (interquartile 17 to 33), not a bias the exponent can remove. A per-design κ from ten cycles is a dead end where it matters most, because LG M50's lever barely moves in ten cycles; on NCA_Kim2011, where it moves 40 to 50 mV, the estimate tracks κ* but reads 6 to 8 V<sup>−1</sup> high. The next test is the one a design search can afford: one κ per parameter set, calibrated on that set's earlier 100-cycle runs (the seen pools give LG M50 about 30 to 57), checked on fresh designs at new currents; and, for the mechanism, whether the steeper lever LG M50 needs equals the ratio of the separator-surface potential rise to the open-circuit lever rise.
  • Caveats: one current per set; κ* uses the cycle-99 loss, so it diagnoses and does not forecast; the estimators were fixed before dev, the hypotheses after it; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/kappa/bench.jsonl, balance.jsonl, ocp.json, dev.txt, dev.json, results.txt, summary.json, kappa.svg; tests tests/test_kappa.py.

2026-11-16 · Milestone 5zf: is the plating law's remaining error in its kinetic exponent κ? Can κ be estimated per design from its first ten cycles, and which κ would each set need? Seen-data diagnosis on the 512 committed designs, then a pre-registered fresh bench (plan, written before any fresh run; H167 to H171 are this entry's)

  • Question: every milestone since 5zb has used κ = αF/RT = 25.3 V<sup>−1</sup> on every set, from OKane2022's plating transfer coefficient (α = 0.65, 298 K). 5ze put the law's remaining error on its structure and named κ as the first candidate. In 5zd's law R<sub>κ</sub>(L) = ∫ exp(κ dU<sub>η</sub>(l)) Q<sub>η</sub>(0)/Q<sub>η</sub>(l) dl the lever dU<sub>η</sub> and the window Q<sub>η</sub> do not depend on κ, so they are tabulated once per design and R<sub>κ</sub> is cheap for any κ (experiments/kappa/run.py).
  • Two ten-cycle estimators, fixed before dev: fit, the κ in [0, 100] V<sup>−1</sup> that makes R<sub>κ</sub>(L<sub>n</sub>), n = 2..10, most nearly a line in n (least 1 − r<sup>2</sup>); slope, the least-squares slope of −[ln ΔL<sub>n</sub> + ln Q<sub>η</sub>(0)/Q<sub>η</sub>(L)] on dU<sub>η</sub>(L) at each cycle's midpoint, n = 3..10. Both use a table over [0, 1.05 L(10)]: 5zd's table spans 30 L(10) in 60 cells, about two cells inside the first ten cycles, which a synthetic test showed biases the slope estimator by 15% (found while writing the tests, before dev; the forecast itself still uses 5zd's table, so κ = 25.3 reproduces 5zd exactly). And one diagnostic that is not a forecast: the oracle κ*, the κ whose cycle-99 forecast is exact (bisection on [0, 100]).
  • Seen (dev; python experiments/kappa/run.py dev, experiments/kappa/dev.txt; 16 pools, 512 designs, every form listed): - The ten-cycle κ does not help. fit forecasts worse than κ = 25.3 on 12 of 16 pools, on all 8 control pools (Ai2020 0.088 to 0.135 against 0.063 to 0.076; NCA_Kim2011 0.057 to 0.065 against 0.018 to 0.029), and better on 4 LG M50 pools by at most 0.020. slope is within 0.03 of fit everywhere. κ = 0 (charge-time lever alone) is 0.25 to 0.41 everywhere, so the potential lever matters. - On LG M50 κ cannot be read from ten cycles: the lever rises by 0.5 to 1.4 mV over cycles 2 to 10 (pool medians), so R is nearly a line for any κ; fit's interquartile range is 49 to 84 V<sup>−1</sup> wide on seven of the eight LG M50 pools, and on the eighth (loaded/Chen2020@1.375x, 16 V<sup>−1</sup>) because more than a quarter of its designs sit at the 100 V<sup>−1</sup> bound (the per-pool count at the bound is the kedge column of dev.txt). Spearman(fit, κ*) is −0.31 to 0.55. - Where the lever moves it can: on NCA_Kim2011 the lever rises 39 to 52 mV in ten cycles and Spearman(fit, κ*) is 0.72 to 0.85, but fit is biased high (29 to 33 against κ* 21 to 24), which is why its forecast is worse. Ai2020 (6 to 8 mV) is in between: Spearman −0.06 to 0.16. - The oracle: LG M50 needs a larger κ, median κ* 30 to 57 V<sup>−1</sup> on all eight LG M50 pools (1.2 to 2.3 × αF/RT); the controls need about the physical one, 20 to 25 (Ai2020) and 21 to 24 (NCA_Kim2011). So the constant η is not the only compensation on LG M50: the law also asks for a steeper potential lever there, and on Ai2020 the oracle median is within 6 V<sup>−1</sup> of 25.3, so its error is scatter in κ* across designs (interquartile 17 to 31) rather than a bias.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 24, used by no milestone; energy-cell bounds) on each of Ai2020@0.5875x, NCA_Kim2011@0.71875x, Chen2020@1.34375x, OKane2022@1.40625x, currents no milestone has used, inside each set's dev range. 128 DFN runs (SEI + plating) to cycle 100 with 5zc's simulate unchanged, 3 workers; memory kills retried with one worker; failed runs dropped and counted.
  • H167 (LG M50 κ is not identifiable from ten cycles): on both LG M50 pools the median lever rise over cycles 2 to 10 is below 2 mV and fit is uninformative, its interquartile range wider than 40 V<sup>−1</sup> or at least a quarter of the designs at a bound of [0, 100]. Refuted if on either the range is under 20 V<sup>−1</sup> with fewer than a quarter at a bound. (The bound clause was added after a first draft of this plan, committed in this PR, used the range alone, which loaded/Chen2020@1.375x already fails in dev; no fresh run had started.)
  • H168 (no ten-cycle gain where it was tried hardest): fit forecasts worse than κ = 25.3 on both control pools. Refuted if better on either.
  • H169 (LG M50 needs a steeper lever): median κ* above 25.3 on both LG M50 pools and above 30 on at least one. Refuted if at most 25.3 on either.
  • H170 (the controls need about the physical κ): median κ* within [17, 28] V<sup>−1</sup> on both control pools. Refuted if outside [12, 35] on either.
  • H171 (identifiable only where the lever moves): Spearman(fit, κ*) at least 0.6 on NCA_Kim2011 and below 0.6 on both LG M50 pools. Refuted if below 0.4 on NCA_Kim2011 or above 0.75 on either LG M50 pool.
  • Caveats fixed now: one current per set; κ* uses the cycle-99 loss, so it diagnoses and does not forecast; the estimators were chosen before dev, the hypotheses after it (all 16 dev pools are in dev.txt); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/kappa/run.py; outcome to be logged above this entry.

2026-11-16 · Milestone 5ze outcome: neither of 5zd's proposed fixes nor a split overpotential removes the Ai2020 cost, and on fresh pools the reason replicates: knowing η's true drift to cycle 99 makes the forecast worse on all four pools (Ai2020 0.111 against 0.063). 5zd's LG M50 result replicates at a new seed (0.109 and 0.095), and the charge-side overpotential from the discharge energy sits within 2 to 5 mV of 5zc's symmetric η, so the symmetric reading was already right. H162 to H166 supported

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 23, 3 workers, about 25 minutes on 4 cores. Three runs (Ai2020@0.6125x designs 3 and 12, OKane2022@1.3125x design 1) were killed for memory (exit −9, not the solver) and re-run with one worker, as the plan fixed; none was dropped, so there are 32 designs per pool. The report was run once, after the bench. experiments/asym/run.py was not changed after the plan.
  • H162 supported (5zd replicates): the η-window law's median |ln(L(99)/L<sub>DFN</sub>(99))| is 0.109 (Chen2020@1.28125x) and 0.095 (OKane2022@1.3125x), against 0.191 and 0.160 for 5zc; Ai2020@0.6125x is 0.063 against 0.024 at open circuit, so 5zd's cost on Ai2020 is still there (signed −0.020, an under-prediction). NCA_Kim2011@0.5625x 0.023 against 0.013: at this lower current the η window is worse than open circuit there too, unlike 5zd's 0.8125× pool.
  • H163 supported: asym's error is within 0.007 of 5zd's on every pool (0.059, 0.023, 0.102, 0.093). It wins 18, 25, 28 and 24 of 32 designs, so the small gain is consistent in sign but not material.
  • H164 supported: median |η<sub>c</sub> − η| is 2.3, 0.8, 5.3 and 3.4 mV.
  • H165 supported: median η<sub>d</sub> is 156, 242 and 256 mV against η<sub>c</sub> 230, 360 and 368 mV on Ai2020, Chen2020 and OKane2022 (NCA_Kim2011 97 against 86, outside the claim as planned). The discharge end carries about two thirds of the charge end's overpotential, and moving it costs little capacity because the OCV is steep there.
  • H166 supported: the oracle drift (η a line in the lost lithium from its ten-cycle mean to the η the cycle-99 charge Ah needs) is worse than a constant η on 4 of 4 pools: 0.111, 0.040, 0.155, 0.126 against 0.063, 0.023, 0.109, 0.095.
  • Descriptive (in the table, not in the plan): from cycles 2 to 10 to cycle 99 the charge-side η<sub>c</sub> falls by 41 mV on Ai2020 (230 to 189), 14 mV on Chen2020 and 7 mV on OKane2022, and rises 32 mV on NCA_Kim2011; η<sub>d</sub> moves by at most 13 mV. So the drift 5zc found is on the charge side. Spearman of the asym forecast against the true cycle-99 loss is 0.981, 1.000, 0.987 and 0.987.
  • Reading: three readings of the overpotential (symmetric, split, and the true drift) give the same or worse forecasts, so the remaining Ai2020 error is not in how η is measured. It sits in the law's structure: a constant η makes the R line through cycles 2 to 10 consistent with the later cycles on LG M50, and putting the true drift in breaks that on every set, which says the constant η is compensating for something the law leaves out (candidates: the kinetic exponent κ, taken from OKane2022's plating parameters on every set, or the electrolyte's share of the potential at the separator). The next test is a ten-cycle estimate of κ per design, from the slowdown of the per-cycle plating over cycles 2 to 10 against the η-window potential rise, checked on the 512 committed designs before a fresh bench.
  • Caveats: one current per set; the oracle uses the cycle-99 charge Ah, so it diagnoses and does not forecast; η<sub>d</sub> assumes the discharge window shares its top with the previous charge (no rest step, as in the protocol); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/asym/bench.jsonl, balance.jsonl, ocp.json, dev.txt, results.txt, summary.json, asym.svg; tests tests/test_asym.py.

2026-11-16 · Milestone 5ze: is 5zd's Ai2020 under-prediction caused by its overpotential drifting, or by the symmetric overpotential 5zc assumed? Seen-data diagnosis of four candidate fixes, then a pre-registered replication on fresh pools of all four sets (plan, written before any fresh run; H162 to H166 are this entry's)

  • Question: 5zd put its Ai2020 cost (2.5% to 7.6%) on η drifting by about −20 mV over 100 cycles and proposed two fixes: let η follow its own ten-cycle trend, or pick open circuit or the η window per design from the first ten cycles. A third assumption is untested: 5zc's η is symmetric, so the charge Ah fixes the window's length but not where it sits, and the potential lever is read at v<sub>hi</sub> − η. The discharge energy fixes the rest: under constant current the mean discharge voltage (Wh over Ah) is the mean open-circuit voltage over the window less η<sub>d</sub>, so two measured numbers per cycle give η<sub>d</sub> and η<sub>c</sub> (experiments/asym/run.py, solve_asym), and the lever is read at v<sub>hi</sub> − η<sub>c</sub>.
  • Seen (dev; python experiments/asym/run.py dev, experiments/asym/dev.txt): 5zb's, 5zc's and 5zd's 384 designs. Five forms, all listed: 5zc (open circuit), 5zd (η window), drift (η a line in the lost lithium through cycles 2 to 10, both levers read at η(L)), select (open circuit or η window, whichever forecasts cycle 10 better from cycles 2 to 7), asym (this plan's split). Plus an oracle that is not a forecast: η(L) a line from its ten-cycle mean to the η the measured cycle-99 charge Ah needs (5zc's and 5zd's pools only). - Drift over-extrapolates: the ten-cycle trend puts LG M50's cycle-99 η at 327 to 347 mV where it needs 347 to 382, and the LG M50 error rises from 0.064 to 0.104 (5zd) to 0.145 to 0.181. Ai2020 improves only to 0.054 to 0.061 from 0.065 to 0.076. - The oracle is worse than a constant η on all eight pools it can be run on, Ai2020 included (0.094 and 0.102 against 0.076 and 0.065; LG M50 0.101 to 0.143 against 0.064 to 0.104). So knowing η's true drift does not fix Ai2020: 5zd's drift explanation does not hold on seen data. The law's constant η works on LG M50 partly by compensation. - Select picks the wrong form: the η window on 28 to 30 of 32 Ai2020 designs (where open circuit is better) and open circuit on 2 to 12 of 32 OKane2022 designs (where the η window is better). Ten cycles do not separate the two readings; they part only later. - Asym: η<sub>c</sub> comes out within 1 to 6 mV of the symmetric η (pool medians), while η<sub>d</sub> is 70 to 150 mV lower on LG M50 and Ai2020 (the bottom of the window is steep in OCV, so it costs little capacity). The forecast moves by at most 0.012 (Chen2020@1.3125x 0.104 to 0.092); Ai2020 is unchanged (0.076 to 0.078). - Also checked (scratch, not committed): plating is 98 to 100% of the lithium lost over cycles 2 to 99 on every seen pool once pl_mol is scaled by the electrodes in parallel (34 on Ai2020), so Ai2020 is a plating cell too; an unscaled first look read 3% and was wrong.
  • No new law is proposed. The fresh bench tests whether these four seen findings replicate at a new seed and new currents, so they can be stated as results rather than dev observations.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 23, used by no milestone; energy-cell bounds) on each of Ai2020@0.6125x, NCA_Kim2011@0.5625x, Chen2020@1.28125x, OKane2022@1.3125x, currents no milestone has used, inside each set's dev range. 128 DFN runs (SEI + plating) to cycle 100 with 5zc's simulate unchanged, 3 workers; memory kills retried; failed runs dropped and counted.
  • H162 (5zd replicates): the η-window law's median |ln(L(99)/L<sub>DFN</sub>(99))| is at most 0.12 on both LG M50 pools, and Ai2020 is above 0.05. Refuted if either LG M50 pool is above 0.15, or if Ai2020 is no worse than open circuit (the cost 5zd found is gone).
  • H163 (asym changes nothing that matters): asym's error is within 0.02 of 5zd's on every pool. Refuted if more than 0.04 away on any.
  • H164 (the charge side carries the overpotential the lever needs): median |η<sub>c</sub> − η| at most 10 mV on every pool. Refuted above 25 mV on any.
  • H165 (the split is real): median η<sub>d</sub> below median η<sub>c</sub> on both LG M50 pools and Ai2020. Refuted if on at most one of the three. (NCA_Kim2011 is not in the claim: dev has η<sub>d</sub> above η<sub>c</sub> at 0.5× and below at the higher currents.)
  • H166 (drift is not the gap): the oracle drift's error is above the constant-η error on at least 3 of 4 pools. Refuted if on at most 1.
  • Caveats fixed now: one current per set; the oracle uses the cycle-99 charge Ah, so it diagnoses and does not forecast; η<sub>d</sub> assumes the discharge window shares its top with the previous charge (no rest step, as in the protocol); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/asym/run.py; outcome logged above this entry.

2026-11-16 · Milestone 5zd outcome: reading the plating law's potential lever at the same η-shortened charge window as its charge-time lever halves the LG M50 forecast error again, from 5zc's 20% and 17% to 10% and 6% on fresh pools (59 of 64 designs won), with no new parameter. The η window also forecasts the cycle-99 separator-surface potential rise better than open circuit there (21 and 17 mV against 35 and 27 mV). The cost is on Ai2020, 2.5% to 7.6%, just past the pre-registered harm bar. H157, H158, H160, H161 supported; H159 mixed

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 22, 3 workers, about 20 minutes on 4 cores. Five Ai2020@0.575x runs were killed for memory (exit −9, not the solver) and re-run with one worker, as the plan fixed; none was dropped, so there are 32 designs per pool. The report was run once, after the bench. experiments/consistent/run.py was not changed after the plan.
  • H157 supported: median |ln(L(99)/L<sub>DFN</sub>(99))| 0.104 and 0.064 against 5zc's 0.202 and 0.167 on Chen2020@1.3125x / OKane2022@1.4375x (30 and 29 of 32 designs won; 5zb: 0.270, 0.259). The over-prediction shrinks from +0.202 and +0.165 (signed) to +0.095 and +0.042.
  • H158 supported: 0.104 and 0.064, both within 0.12.
  • H159 mixed: NCA_Kim2011@0.8125x improves, 0.033 to 0.020 (26 of 32 won). Ai2020@0.575x worsens from 0.025 to 0.076 (signed +0.006 to −0.060, now an under-prediction), by 0.051: past the 0.05 bar and inside the 0.10 refutation line. Dev had said about 0.04.
  • H160 supported: worst pool 0.104 (Chen2020) against 5zc's 0.202 (Chen2020). Over the programme's fresh pools the worst-pool error has gone 0.346 (5y), 0.264 (5zb), 0.210 (5zc), 0.104 (here).
  • H161 supported: median absolute error of the predicted cycle-99 separator-surface OCP rise (measured median 39 and 36 mV) is 21.1 and 16.6 mV against 35.0 and 27.3 mV at open circuit. On the controls the η window is about as poor as open circuit (Ai2020 75 against 80 mV of a 118 mV rise) or worse (NCA_Kim2011 40 against 23 mV).
  • Descriptive (not in the plan; computed from summary.json after the verdicts): Spearman of the predicted against the true cycle-99 loss falls on LG M50, 0.994 to 0.971 (Chen2020) and 0.964 to 0.942 (OKane2022), and is 0.990 and 1.000 on the controls (5zc 0.996, 0.997). So the η lever fixes the size of the loss more than its order across designs.
  • Reading: on LG M50 the programme's ten-cycle plating forecast is now inside 10% with every input either the parameter set, the design's balance, or its own first ten cycles of loss and charge Ah. The two levers of 5zb's kinetics are both read where the loaded charge actually ends, set by one effective overpotential. On Ai2020 the same reading over-corrects: its η drifts by about −20 mV over 100 cycles (5zc, H156), so the shortened window over-states the late potential rise and the law under-predicts. The next test is whether letting η follow its own ten-cycle trend (one more number from the same cycles) removes the Ai2020 under-prediction without giving back the LG M50 gain, or whether a per-set rule (open circuit where the charge Ah already matches, the η window where it does not) can be stated in advance from the first ten cycles.
  • Caveats: one current per set; one symmetric η held constant; the form was chosen after 256 seen designs and seven forms (all in dev.txt); four pools; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/consistent/bench.jsonl, balance.jsonl, ocp.json, dev.txt, results.txt, summary.json, consistent.svg; tests tests/test_consistent.py.

2026-11-16 · Milestone 5zd: does 5zc's loaded law forecast the 100-cycle lithium loss better when its potential lever is read at the same η-shortened charge window as its charge-time lever? Fresh pools of all four sets (plan, written before any fresh run; H157 to H161 are this entry's)

  • Question: 5zc moved the charge-time lever to the loaded window (the charge stops when the open-circuit voltage is η short of the upper cut-off) and cut LG M50's over-prediction to 21% and 16%, but kept the potential lever dU at the open-circuit upper cut-off. Its post hoc put the remaining gap on the surface potential at the separator. If the charge stops at OCV = v<sub>hi</sub> − η, the negative electrode's open-circuit stoichiometry at the end of each charge is the top of that shortened window, so the consistent reading of the potential lever is dU<sub>η</sub>(L) = U<sub>n</sub>(x<sub>hi</sub>(n<sub>Li</sub> − L; v<sub>hi</sub> − η)) − U<sub>n</sub>(x<sub>hi</sub>(n<sub>Li</sub>; v<sub>hi</sub> − η)). One η (5zc's, from the charge Ah of cycles 2 to 10) then sets both levers; nothing is fitted beyond 5zc's line in n.
  • Model, fixed now (experiments/consistent/run.py): R = ∫ exp(κ dU<sub>η</sub>) Q<sub>η</sub>(0)/Q<sub>η</sub>(l) dl, κ = 25.3 V<sup>−1</sup>, a line in n through cycles 2 to 10, read at 99, inverted. Inputs: the parameter set, the design's balance, its first ten cycles' loss and charge Ah. The separator-surface OCP is not an input; it is used only to score H161.
  • Seen (dev; python experiments/consistent/run.py dev, experiments/consistent/dev.txt): 5zb's and 5zc's 256 designs. Seven potential-lever forms were tried, all listed in dev.txt: open circuit (5zc), open circuit plus 5za's stoichiometry offset, the η window (this plan), the η window plus an offset, a line in L through the measured surface OCP, and the open-circuit and η rises scaled through the origin to the measured cycles 2 to 10 rise. Median |ln(L(99)/L<sub>DFN</sub>(99))|, 5zc against the η window: Chen2020@1.25x 0.192 to 0.102, Chen2020@1.375x 0.210 to 0.080, OKane2022@1.25x 0.161 to 0.097, OKane2022@1.375x 0.161 to 0.071; controls Ai2020@0.525x 0.031 to 0.065, Ai2020@0.65x 0.021 to 0.065, NCA_Kim2011@0.5x 0.025 to 0.029, NCA_Kim2011@0.6875x 0.023 to 0.018. The η window forecasts the cycle-99 surface OCP rise better than open circuit on all four LG M50 pools (16 to 20 mV against 26 to 30 mV median error) but worse on three of four controls. The offset forms forecast the rise best (5 to 13 mV on LG M50) yet give worse loss forecasts, so a better rise forecast alone does not buy a better loss forecast; the η window was chosen because it adds no parameter and follows from 5zc's own assumption, not only because it scored best.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 22, used by no milestone; energy-cell bounds) on each of Ai2020@0.575x, NCA_Kim2011@0.8125x, Chen2020@1.3125x, OKane2022@1.4375x, currents no milestone has used, inside each set's dev range. 128 DFN runs (SEI + plating) to cycle 100 with 5zc's simulate unchanged, 3 workers; memory kills retried; failed runs dropped and counted.
  • H157 (LG M50, better): the η-window law's median |ln err| is below 5zc's on both LG M50 pools. Refuted if on neither.
  • H158 (LG M50, good enough): at most 0.12 on both LG M50 pools. Refuted above 0.15 on either (5zc's H153 bar, missed by 5zc).
  • H159 (controls, bounded harm): no worse than 5zc by more than 0.05 on either control pool. Refuted if worse by more than 0.10 on either. Dev says Ai2020 will be worse by about 0.04.
  • H160 (one law): the worst pool error over the four pools is below 5zc's worst. Refuted otherwise.
  • H161 (the lever itself): the η window forecasts the cycle-99 separator-surface OCP rise u(99) − u(2) with a smaller median absolute error than the open-circuit reading on both LG M50 pools. Refuted if on neither.
  • Caveats fixed now: one current per set; one symmetric η held constant over 100 cycles (5zc's H156 found it drifts by 20 to 35 mV on the controls); the form was chosen after seeing 256 designs and seven forms; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/consistent/run.py; outcome logged above this entry.

2026-11-16 · Milestone 5zc outcome: reading the charge time from the loaded charge capacity (an effective overpotential η measured in the design's first ten cycles) cuts 5zb's LG M50 over-prediction of the 100-cycle lithium loss from 28% and 25% to 21% and 16%, wins on all 64 LG M50 designs, and leaves the controls at 3.0% and 2.3%. A constant η predicts the cycle-99 charge Ah within 4 to 5% on three pools (7% on Ai2020), where the open-circuit capacity is off by 20 to 86%. Post hoc, the measured charge Ah plus the measured separator-surface potential rise make LG M50's per-cycle plating steady, so the gap left is forecasting that surface rise. H152, H154, H155 supported; H153, H156 mixed

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 21, 3 workers, about 17 minutes on 4 cores, none failed or killed; 32 designs per pool. The report was run once, after the bench. experiments/loaded/run.py was changed after the plan only to add the post-hoc command below; the analysis is untouched.
  • H152 supported: median |ln(L(99)/L<sub>DFN</sub>(99))| 0.210 and 0.161 against 5zb's 0.279 and 0.248 on Chen2020@1.375x / OKane2022@1.375x, 32 of 32 designs won on each. Both still over-predict (signed +0.210, +0.161).
  • H153 mixed: OKane2022 0.161 and Chen2020 0.210, above the 0.15 bar and below the 0.22 refutation line (dev: 0.193, 0.161).
  • H154 supported: Ai2020@0.525x 0.030 against 0.031 (18 of 32 won; signed −0.004 against +0.027), NCA_Kim2011@0.6875x 0.023 against 0.018 (+0.005, inside the 0.02 margin; 8 of 32 won).
  • H155 supported: worst pool 0.210 (Chen2020) against 5zb's 0.279 (Chen2020); 5y's worst was 0.346. Spearman of the predicted against the true cycle-99 loss 0.982, 0.995, 0.995, 0.996.
  • H156 mixed: with η held at its cycles 2 to 10 value, Q<sub>η</sub> at the cycle-99 lithium misses the cycle-99 charge Ah by a median |ln| 0.069, 0.047, 0.048 and 0.040 (Ai2020, NCA_Kim2011, Chen2020, OKane2022); the open-circuit capacity misses by 0.287, 0.196, 0.831 and 0.856. The η the cycle-99 charge needs is 162, 147, 372 and 377 mV against 182, 112, 378 and 383 mV from cycles 2 to 10, so η is nearly constant on LG M50 and drifts on the controls (−20 mV on Ai2020, +35 mV on NCA_Kim2011).
  • Descriptive (in the plan): with 5za's surface offset as well, 0.141, 0.113, 0.239 and 0.153; it helps neither control and only OKane2022.
  • Post hoc (after the verdicts; python experiments/loaded/run.py posthoc, experiments/loaded/posthoc.txt): median ln of the per-cycle loss at cycle 99 over cycle 2 is −1.91, −4.43, −1.33, −1.30. Removing the measured charge-Ah change and κ times the open-circuit potential rise leaves −0.23, −0.07, −0.78, −0.58; removing the charge Ah and κ times the measured separator-surface OCP rise (5z's lever) leaves +1.35, −0.49, −0.14, +0.06. So on LG M50 the charge time and the surface potential together carry the whole slowdown (the rate is steady to within 15%), while on the controls the open-circuit rise does. The NCA_Kim2011 open-circuit figure is sensitive to which cycle's lithium dU is read at (−0.07 at the lithium before each cycle, −0.49 one cycle later), because its loss per cycle falls 80-fold.
  • Reading: the charge-time lever is now read correctly. A constant effective overpotential turns ten cycles of charge Ah into a 100-cycle charge capacity within 5% on LG M50, where the open-circuit balance is off by a factor of 2.3. Its cost on the controls is nil. What remains on LG M50 is the potential lever: the plating slows through the loaded surface OCP at the separator, which the open-circuit dU under-reads and 5za's ten-cycle offset predicts poorly. The next test is a ten-cycle forecast of that surface rise, checked against the 128 recorded u_end curves here before any fresh bench.
  • Caveats: one current per set; one symmetric η, an effective number, not a measured overpotential; open-circuit dU; the form was proposed by 5zb's post hoc and checked on 5zb's pools (seen; one form tried); four pools; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/loaded/bench.jsonl, balance.jsonl, ocp.json, dev.jsonl, dev.txt, results.txt, summary.json, posthoc.txt, loaded.svg; tests tests/test_loaded.py.

2026-11-16 · Milestone 5zc: does 5zb's kinetic law forecast the 100-cycle lithium loss better when the charge time is read from the loaded charge capacity, measured in the design's own first ten cycles, instead of the open-circuit capacity? Fresh pools of all four sets (plan, written before any fresh run; H152 to H156 are this entry's)

  • Question: 5zb's post hoc found the loaded charge on LG M50 shrinks faster than the open-circuit capacity Q(L) its law uses (discharge-energy ratio 0.61 against Q ratio 0.72 by cycle 100), so the charge-time lever is under-read and the law over-predicts by 24 to 26%. 5zb proposed the loaded capacity in place of Q.
  • Model, fixed now (experiments/loaded/run.py): under constant-current charge the charge stops when the open-circuit voltage is η short of the upper cut-off, and the discharge before it stopped η above the lower one. Q<sub>η</sub>(L) is the open-circuit capacity between v<sub>lo</sub> + η and v<sub>hi</sub> − η with n<sub>Li</sub> − L of lithium (5r's balance). Per design, η is solved (bisection) so that Q<sub>η</sub> equals the measured charge Ah of cycle n, n = 2..10, and averaged; then 5zb's law unchanged with Q<sub>η</sub> for Q: R = ∫ exp(κ dU) Q<sub>η</sub>(0)/Q<sub>η</sub>(l) dl, κ = 25.3 V<sup>−1</sup>, open-circuit dU, a line in n through cycles 2 to 10, read at 99, inverted. Inputs: the parameter set, the design's balance, its first ten cycles' loss and charge Ah. One symmetric η per design is the assumption under test (H156); it is an effective number, not a measured overpotential.
  • Seen (dev; python experiments/loaded/run.py dev, then devreport, experiments/loaded/dev.txt): 5zb's 128 designs re-run to cycle 10 for the charge Ah (their lithium loss over cycles 1 to 10 reproduces 5zb's committed curves exactly, max relative difference 0), scored against 5zb's committed 100-cycle curves. Median |ln(L(99)/L<sub>DFN</sub>(99))|, 5zb against loaded: Ai2020@0.65x 0.076 to 0.021 (24 of 32 designs win), NCA_Kim2011@0.5x 0.024 to 0.025 (6 of 32), Chen2020@1.25x 0.264 to 0.193 (32 of 32), OKane2022@1.25x 0.243 to 0.161 (32 of 32). Median η 251, 74, 345 and 351 mV. Only this one form was tried. With 5za's surface offset as well (descriptive): 0.173, 0.025, 0.165, 0.139.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 21, used by no milestone; energy-cell bounds) on each of Ai2020@0.525x, NCA_Kim2011@0.6875x, Chen2020@1.375x, OKane2022@1.375x, currents no milestone has used, inside each set's dev range. 128 DFN runs (SEI + plating) to cycle 100 with 5za's simulate plus the charge and discharge Ah per cycle, 3 workers; memory kills retried; failed runs dropped and counted.
  • H152 (LG M50, better): the loaded law's median |ln err| is below 5zb's on both LG M50 pools. Refuted if on neither.
  • H153 (LG M50, good enough): at most 0.15 on both LG M50 pools. Refuted above 0.22 on either. Dev (0.19, 0.16) says this is not expected to pass on Chen2020.
  • H154 (controls, no harm): no worse than 5zb by more than 0.02 on either control pool. Refuted if worse by more than 0.05 on either.
  • H155 (one law): the worst pool error is below 5zb's worst pool error over the four pools. Refuted otherwise.
  • H156 (the model's own check): with η held at its cycles 2 to 10 value, Q<sub>η</sub> at the cycle-99 lithium predicts the cycle-99 charge Ah within median |ln| 0.05 on all four pools. Refuted above 0.10 on any.
  • Caveats fixed now: one current per set; one symmetric η held constant over 100 cycles; open-circuit dU, which 5z showed is the wrong place on LG M50; the form was proposed by 5zb's post hoc and checked on 5zb's pools (seen); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/loaded/run.py; outcome logged above this entry.

2026-11-16 · Milestone 5zb outcome: a ten-cycle law whose shape is fixed by the plating kinetics (plating per cycle proportional to the charge capacity, slowed by the negative potential rise, so a line in the cycle count) beats 5y's power law on all four fresh pools, 122 of 128 designs, and halves or better its error on the controls (Ai2020@0.65x 0.150 to 0.076, NCA_Kim2011@0.5x 0.078 to 0.024). One law now serves every set, with the worst pool at 0.264 against 0.325. LG M50 is still over-predicted by 24 to 26%. H147, H149, H150, H151 supported; H148 mixed

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 20, 3 workers, about 16 minutes on 4 cores. One Ai2020@0.65x run was killed for memory (exit −9, not the solver) and re-run with one worker. No design was dropped, so there are 32 per pool. The report was run once, after the bench. experiments/kinetic/run.py was not changed after the plan.
  • H147 supported: median |ln(L(99)/L<sub>DFN</sub>(99))| is 0.076 against 5y's 0.150 on Ai2020@0.65x (31 of 32 designs won) and 0.024 against 0.078 on NCA_Kim2011@0.5x (30 of 32).
  • H148 mixed: NCA_Kim2011@0.5x is within the 0.06 bar. Ai2020@0.65x is 0.076 (signed +0.062, an over-prediction), above the bar and below the 0.10 refutation line. 0.65× is outside the dev range, and the over-prediction grows with current, as it did on the dev pools (Ai2020 signed −0.008 at 0.3× to +0.032 at 0.6×; NCA_Kim2011 −0.024 at 0.5× to +0.059 at 1×).
  • H149 supported: 0.264 and 0.243 against 0.308 and 0.325 on Chen2020@1.25x / OKane2022@1.25x (29 and 32 wins), both above 0.15.
  • H150 supported: the worst pool is 0.264 (Chen2020@1.25x) against 5y's 0.325 (OKane2022@1.25x). Across the four pools the kinetic law wins 4 of 4 (one-sided sign p = 0.0625) and 122 of 128 designs.
  • H151 supported: Spearman of the predicted against the true cycle-99 loss is 0.977, 0.999, 0.991 and 0.993 (5y: 0.962, 1.000, 0.995, 0.994).
  • Descriptive (in the plan): with 5za's surface offset the kinetic law gives 0.204 and 0.179 on the LG M50 pools, the best so far there (5za: 0.21 to 0.23 on other pools), but 0.142 on Ai2020 (signed −0.142), so the surface reading still hurts the control.
  • Post hoc (after the verdicts): the discharge energy at cycle 100 over cycle 2 is 0.605 and 0.607 on the LG M50 pools, while the open-circuit capacity ratio the law uses is 0.723 and 0.732. On Ai2020 the two agree to within 0.03 (0.556 against 0.579), and on NCA_Kim2011 they are 0.461 against 0.425. So on LG M50 the loaded charge shrinks faster than the open-circuit capacity says, the charge-time lever is under-read, and the law over-predicts, which is the direction of the residual.
  • Reading: once the charge time is in the feedback, the plating kinetics fix the law's shape, and no curvature needs fitting. That removes 5za's double count on Ai2020 and works at a current and seed no milestone had seen. The 5y power law worked through compensation, and so the kinetic law transfers better (worst pool 0.26 against 0.33, controls 2 to 3× better). The LG M50 gap is now two named under-reads: the potential rise at the separator surface (5z/5za) and the loaded charge capacity (here). Both are visible in the first ten cycles of the design's own run. The next test is the law with the loaded charge capacity per cycle in place of the open-circuit Q, plus the surface offset, pre-registered on all four sets.
  • Caveats: one current per set; Q is the open-circuit capacity; open-circuit dU; the form was chosen after seeing 5za's pools and all 13 dev pools (8 forms tried, all listed in the plan); four pools (sign p = 0.0625); OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/kinetic/bench.jsonl, balance.jsonl, ocp.json, dev.txt, results.txt, summary.json, kinetic.svg; tests tests/test_kinetic.py.

2026-11-16 · Milestone 5zb: does a ten-cycle law whose shape comes from the plating kinetics, not from a fitted power law, forecast the 100-cycle lithium loss on fresh pools of all four parameter sets? One law, a fitted level and rate only (plan, written before any fresh run; H147 to H151 are this entry's)

  • Question: 5za found 5y's open-circuit predictor works on Ai2020 and NCA_Kim2011 partly by compensation: the power law fitted to R through ten cycles carries part of the deceleration, so an accurate feedback counts it twice. 5za proposed fixing the law's shape from the kinetics. The kinetics give two levers, not one: PyBaMM's irreversible plating current, slowed by the negative potential rise (5x), integrated over a charge that lasts Q(L)/I at constant current, Q(L) the open-circuit capacity between the cut-offs with n<sub>Li</sub> − L of lithium. With an otherwise steady rate, dL/dn = r<sub>0</sub> (Q(L)/Q(0)) exp(−κ dU(L)), so R<sub>Q</sub>(L) = ∫<sub>0</sub><sup>L</sup> exp(κ dU(l)) Q(0)/Q(l) dl is linear in the cycle count, and the law's curvature is no longer free.
  • Diagnostic on 5za's committed curves (seen; scratch script, not committed): with the measured separator-surface OCP as the feedback, the per-cycle plating divided by exp(−κ ΔU<sub>meas</sub>) still falls from cycle 2 to 99 by ln −0.59 and −0.52 on the LG M50 pools and −1.71 on NCA_Kim2011@0.875x (+0.21 on Ai2020@0.45x); dividing also by the discharge-energy ratio (a charge-time proxy, ln −0.42 to −0.67) leaves −0.18, −0.08, −1.07, +0.99. So the potential alone does not make the rate steady, and the charge time is a lever of the same size.
  • Forms tried on 5za's 128 seen curves, all disclosed (median |ln(L(99)/L<sub>DFN</sub>(99))| on Chen2020@1.5x, OKane2022@1.5x, NCA_Kim2011@0.875x, Ai2020@0.45x): 5y 0.351, 0.358, 0.030, 0.085; 5za 0.231, 0.209, 0.065, 0.220; a line in n through 5za's surface R, cycles 2 to 10: 0.236, 0.195, 0.299, 0.135; the same through cycles 5 to 10: 0.258, 0.223, 0.256, 0.197; a line through the open-circuit R: 0.401, 0.362, 0.088, 0.196; a line through R<sub>Q</sub> with the surface offset: 0.200, 0.175, 0.206, 0.098; the power law on that R<sub>Q</sub>: 0.210, 0.191, 0.058, 0.084; a line through the open-circuit R<sub>Q</sub>: 0.297, 0.250, 0.043, 0.031. The last is the only form that fixes the shape and needs nothing but the parameter set, the design's balance and its first ten cycles' loss, so it is the predictor tested here; the surface variant is reported, not counted.
  • Dev on all 13 committed 100-cycle pools (seen; python experiments/kinetic/run.py dev, experiments/kinetic/dev.txt): the kinetic law against 5y, median |ln err|: Ai2020 at 0.3, 0.35, 0.4, 0.45, 0.5, 0.55, 0.6× 0.026 to 0.033 against 0.080 to 0.105, winning on 53/53, 60/60, 64/64, 61/62, 62/63, 64/64, 64/64 designs; NCA_Kim2011 0.017 and 0.022 against 0.056 and 0.038 at 0.625 and 0.75×, but 0.043 and 0.059 against 0.031 and 0.024 at 0.875 and 1× (now over-predicting, +0.04, +0.06); LG M50 at 1.5× 0.305 and 0.256 against 0.358 and 0.351.
  • Predictor, fixed now (experiments/kinetic/run.py, kinetic_loss): per design, R<sub>Q</sub> tabulated on 0 ≤ L ≤ min(0.95 n<sub>Li</sub>, 30 L(10)) with 5x's open-circuit dU at the upper cut-off and Q from 5r's balance (60-point midpoint rule), κ = 25.3 V<sup>−1</sup>; a least-squares line through R<sub>Q</sub>(L(n)) for n = 2..10, read at n = 99, inverted. Baseline: 5y's power law on R, unchanged.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 20, used by no milestone; energy-cell bounds) on each of Ai2020@0.65x, NCA_Kim2011@0.5x, Chen2020@1.25x, OKane2022@1.25x, a current per set that no milestone has run to cycle 100 (Ai2020 at 0.65× is outside the dev range of 0.3 to 0.6×). 128 DFN runs (SEI + plating) to cycle 100 with 5za's simulate, unchanged, 3 workers; memory kills retried; failed runs dropped and counted.
  • H147 (controls, better): the kinetic law's median |ln err| is below 5y's on both control pools (Ai2020, NCA_Kim2011). Refuted if on neither.
  • H148 (controls, good): at most 0.06 on both control pools. Refuted above 0.10 on either.
  • H149 (LG M50, better but not enough, as dev says): below 5y's on both LG M50 pools and above 0.15 on both. Refuted if below 5y's on neither.
  • H150 (one law): the kinetic law's worst pool error is below 5y's worst pool error over the four pools. Refuted otherwise.
  • H151 (order): Spearman of the predicted against the true cycle-99 loss at least 0.9 on all four pools. Refuted below 0.8 on any.
  • Caveats fixed now: one current per set; Q is the open-circuit capacity, not the loaded charge time; open-circuit dU, which 5z showed is the wrong place on LG M50; the form was chosen after seeing 5za's pools and all 13 dev pools; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/kinetic/run.py; outcome logged above this entry.

2026-11-16 · Milestone 5za outcome: read at the separator-side surface, the plating feedback cuts 5y's over-prediction of the 100-cycle lithium loss on fresh LG M50 pools from 35% to 21 to 23%, with no constant fitted, but not to the 15% bar; on the controls it does harm, and on Ai2020 it does harm while predicting the surface rise exactly, so 5y's open-circuit reading works there partly by compensation. The Ai2020 bookkeeping gap is the parallel-electrode count (5p), confirmed on 32 fresh designs. H143, H145, H146 supported; H144 mixed

  • Bench: 128 DFN runs (SEI + plating) to cycle 100, Sobol seed 19, 3 workers, about 25 minutes on 4 cores. Four Ai2020@0.45x runs were killed for memory (exit −9, not the solver) and re-run with one worker; none dropped, 32 designs per pool. The report was run once, after the bench; experiments/surface/run.py was changed after the plan only to retry memory kills (the analysis is untouched).
  • H143 supported: median |ln(L(99)/L_DFN(99))| 0.231 and 0.209 against 5y's 0.351 and 0.358 on Chen2020@1.5x / OKane2022@1.5x; the surface predictor wins on 20 and 23 of 32 designs. Both still over-predict (signed +0.231, +0.209).
  • H144 mixed: above the 0.15 bar on both pools, below the 0.25 refutation line on both (dev: 0.128, 0.130; the fresh pools are worse than the seen ones).
  • H145 supported (the predicted failure): worse than 5y on both controls, NCA_Kim2011@0.875x 0.065 against 0.030 and Ai2020@0.45x 0.220 against 0.085 (wins 4 and 1 of 32).
  • H146 supported: Spearman of the predicted against the true cycle-99 loss 0.959 and 0.962 (5y: 0.987, 0.984, so order was never the problem).
  • Bookkeeping, as planned: plating is 99.8%, 99.8%, 98.9% and 99.6% of the cycle-99 loss once PyBaMM's booked plating and SEI are multiplied by the parallel-electrode count (34 on Ai2020, 1 elsewhere); total lost / (count × booked) is 1 to five decimals on all 128 runs.
  • Post hoc (after the verdicts, from the recorded surface OCP): the measured rise of the separator-node surface OCP from cycle 2 to 99 is a median 26.4 and 25.8 mV on the LG M50 pools, against 18.8 and 18.1 mV predicted by the shifted OCP table; on Ai2020 88.7 mV measured against 89.2 predicted; on NCA_Kim2011 102 against 59. The open-circuit reading predicts 0.6, 8.9, 130 and 39 mV.
  • Reading: on LG M50 the surface offset puts the predictor on the right lever (a rise appears where the open-circuit reading sees none) and removes a third of the error, but it under-reads the rise (19 against 26 mV) because the offset taken from cycles 2 to 10 shrinks as the charge shortens, so the loss is still over-predicted. On Ai2020 the predicted rise is right and the forecast is worse: the power law fitted to R over cycles 2 to 10 already carries part of the deceleration, so an accurate feedback counts it twice, the same double count 5x met with the √n law. So 5y's open-circuit predictor is not the physics read correctly on Ai2020 and NCA_Kim2011; it is a feedback that is too weak, paired with a law that is too curved. A predictor faithful to the mechanism needs the law's shape fixed by the plating kinetics (a feedback-free rate taken from cycle 1 or 2 only, not a power law fitted through ten cycles), which is the next test.
  • Caveats: two LG M50 pools at one current; δ averaged over cycles 2 to 10 at one node; the form was chosen on 5z's seen designs; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/surface/bench.jsonl, dev.jsonl, dev.txt, results.txt, summary.json, surface.svg; tests tests/test_surface.py.

2026-11-16 · Milestone 5za: does 5y's ten-cycle predictor work on the LG M50 sets once the plating feedback is read at the separator-side particle surface instead of at open circuit? Fresh Sobol pools, no constant fitted (plan, written before any fresh run; H143 to H146 are this entry's)

  • Question: 5z found the plating slows on the LG M50 sets (Chen2020, OKane2022) through the negative OCP at the loaded surface by the separator (+38 mV by cycle 99), where 5x/5y's open-circuit reading sees 0.5 to 9 mV and 5y over-predicts the cycle-99 loss by about 35%. 5z proposed predicting that surface shift from the first ten cycles.
  • Correction to 5z, found while planning: 5z's descriptive note that on Ai2020 only 3% of the loss is booked to plating or SEI is the parallel-electrode bookkeeping that 5p already measured and documented (experiments/attribution/UPSTREAM.md): PyBaMM 26.10.1.1 books SEI and plating per electrode pair (L_y L_z) but totals lithium over A_cc = L_y L_z n_parallel, and Ai2020 has 34 electrodes in parallel. A 3-cycle re-run of 5z's Ai2020@0.45x design 7 gives lost 0.0053285 mol, booked 0.00015672 mol, ratio 34.000; plating alone (SEI off) gives the same ratio. Times 34, plating is 99.7% of that loss. So the Ai2020 loss 5u to 5y fitted is plating, as on the other sets, and 5z's "needs resolving before Ai2020 counts as a second cell" is withdrawn. This bench records the count and reports the corrected share per pool.
  • Seen (dev; python experiments/surface/run.py dev, experiments/surface/dev.txt): 5z's 39 designs re-run to cycle 10 for the separator-node surface stoichiometry at end of charge, scored against 5z's committed 100-cycle curves. The 5z trajectories show the surface OCP flat for the first 10 to 20 cycles on LG M50 and rising between cycles 30 and 75, so a slope fitted to ten cycles of the surface OCP would see nothing; the predictor instead takes the surface-over-bulk offset at end of charge and lets the set's OCP table say when the shifted stoichiometry leaves the plateau. Median |ln(L(99)/L_DFN(99))|: 5y 0.340 and 0.346, surface 0.128 and 0.130 on Chen2020@1.5x / OKane2022@1.5x (wins 8/12, 11/12; offset δ −0.098, −0.111; still over-predicting, +0.115, +0.101). On the controls the surface reading is worse: NCA_Kim2011@0.875x 0.020 to 0.047, Ai2020@0.45x 0.077 to 0.229 (δ +0.17, +0.21). Only this one form was tried.
  • Predictor, fixed now (experiments/surface/run.py): per design, δ = mean over cycles 2 to 10 of x<sub>surf</sub>(separator node, end of charge) − x1(n<sub>Li</sub> − L), x1 the open-circuit upper-cut-off stoichiometry (5r's balance table); dU<sub>s</sub>(L) = U<sub>n</sub>(x1(n<sub>Li</sub> − L) + δ) − U<sub>n</sub>(x1(n<sub>Li</sub>) + δ); then 5y unchanged: R = ∫ exp(κ dU<sub>s</sub>) dl, κ = 25.3 V<sup>−1</sup>, power law on R over cycles 2 to 10, read at cycle 99, inverted. Inputs: the parameter set, the design's balance, its first ten cycles.
  • Fresh pools, fixed now: 32 scrambled Sobol designs (seed 19, used by no milestone; energy-cell bounds) on each of Chen2020@1.5x, OKane2022@1.5x and controls NCA_Kim2011@0.875x, Ai2020@0.45x, 128 DFN runs (SEI + plating) to cycle 100, one fresh process per run, 3 workers. Failed runs are dropped and counted.
  • H143 (better): the surface predictor's median |ln err| is below 5y's on both LG M50 pools. Refuted if on neither.
  • H144 (good enough): at most 0.15 on both LG M50 pools. Refuted if above 0.25 on either.
  • H145 (not universal, as dev says): worse than 5y by more than 0.03 on both controls. Refuted if no worse than 5y on either.
  • H146 (order): the surface predictor ranks the true cycle-99 loss at Spearman 0.9 or above on both LG M50 pools. Refuted below 0.8 on either.
  • Caveats fixed now: two LG M50 pools at one current; δ averaged over cycles 2 to 10 at one node; the form was chosen on 5z's seen designs; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/surface/run.py; outcome logged above this entry.

2026-11-16 · Milestone 5z outcome: on the LG M50 sets the plating slows for the same reason as on NCA_Kim2011, the negative electrode's open-circuit potential rising, but at the loaded surface by the separator (+38 mV at end of charge by cycle 99), not in the open-circuit window 5x read (0.5 to 9 mV). Plating is 99.8% of the loss there; a one-node rate index tracks the per-cycle plating change within 0.015. On Ai2020 only 3% of the recorded loss is booked to plating or SEI. H139, H140, H142 supported; H141 refuted

  • Bench: 40 DFN runs (SEI + plating) to cycle 100, 3 workers, about 4 minutes on 4 cores; 1 killed for memory (Ai2020@0.45x design 7, exit −9, not retried), so 12, 12, 8 and 7 designs scored. The report was run once, after the bench finished; experiments/mechanism/run.py was not changed after the plan.
  • H139 supported: plating is 99.8% (median) of the lithium lost by cycle 99 on both LG M50 pools, at least 90% on every design; SEI 0.2%.
  • H140 supported: median |ln(index<sub>99</sub>/index<sub>2</sub>) − ln(ΔP<sub>99</sub>/ΔP<sub>2</sub>)| is 0.015 and 0.014 on Chen2020@1.5x and OKane2022@1.5x (the per-cycle plating falls by ln −1.23 and −1.18, about 3.3×). Reported, not counted: 0.069 on Ai2020@0.45x, 0.49 on NCA_Kim2011@0.875x, where the single node misses part of the decay.
  • H141 refuted: the surface-OCP term carries the change everywhere. Median −κΔU<sub>surf</sub> is −0.95 and −0.97 on the LG M50 pools, 1.16 and 1.20 times the end-of-charge exponent change (−0.77, −0.73), against 1.03 on NCA_Kim2011 (−2.70 of −2.64). The surface OCP at the separator rises 37.5 and 38.4 mV by cycle 99 on LG M50 (5x's open-circuit ΔU: 0.5 and 8.9 mV), 107 mV on NCA_Kim2011, 78 mV on Ai2020. Partly offsetting: the intercalation overpotential grows more negative (−7.6, −9.4 mV, +0.19 and +0.24 log units); film and c<sub>e</sub> terms are under 0.07. The charge gets shorter (ln t −0.43), which the index carries apart from the end-of-charge terms.
  • H142 supported: every re-run reproduces the committed cycle-99 lithium loss to better than 0.01% (largest |difference| 0.0000 at four places).
  • Descriptive, not planned: on Ai2020@0.45x the lithium booked to plating is 2.9% of PyBaMM's "Total lithium lost [mol]" at cycle 99 and SEI 0.0%. A 3-cycle check on design 0 (after the report) shows 0.0053 mol lost from the particles against 0.00016 mol to side reactions with SEI + plating on, and none lost with both off. So the loss 5u to 5y fitted on Ai2020 is mostly lithium leaving the particles without being booked to any side reaction in PyBaMM 26.10.1.1's accounting; on the other three sets the two agree (plating + SEI 98.7 to 100%). Its source is not identified here.
  • Reading: the open-circuit window is the wrong place to read the plating feedback on a cell whose graphite is on a plateau at rest. Under charge the separator-side surface runs ahead of the bulk, past the plateau, and lost lithium moves it back down a steep part of the OCP curve; that is a 38 mV lever where the open-circuit window shows 0.5 mV. 5x's mechanism is then one law for all three plating-dominated sets, with the surface stoichiometry at the separator at end of charge in place of the open-circuit x1. The next step is to predict that surface shift from the first ten cycles (it is observed in each of them) and rerun 5x/5y's predictor with it, pre-registered on fresh LG M50 pools. On Ai2020 the fitted loss is not plating, so the 5u to 5y results there are about a quantity whose physics this milestone has not named; that needs resolving before Ai2020 counts as a second cell.
  • Caveats: 39 designs, all seen at the aggregate level; one node at end of charge summarises a profile in x and t (it misses 0.49 of 4.4 log units on NCA_Kim2011); the shares are of the end-of-charge exponent, not of the time-integrated rate; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/mechanism/bench.jsonl, results.txt, summary.json; tests tests/test_mechanism.py.

2026-11-16 · Milestone 5z: on the LG M50 sets, what slows the lithium loss? A decomposition of PyBaMM's plating exponent at the separator-side node, cycle 2 against cycle 99, on re-run designs of committed pools (plan, written before the bench; H139 to H142 are this entry's)

  • Question: 5x's parameter-free correction (the plating exponential through the negative electrode's open-circuit potential at top of charge) works on NCA_Kim2011 and predicts no feedback on Chen2020 / OKane2022 (ΔU 0.5 and 8.9 mV), yet on 5w's two LG M50 pools the per-cycle loss falls about threefold from cycle 2 to cycle 99 (dev below). The ten-cycle laws miss by −33% (√n) and +44% (power law), so neither carries the shape. To derive a law for these sets the mechanism must be named first.
  • Dev, seen (stdlib, the 13 committed 100-cycle pools, scratch scripts not committed): fitted to cycles 2 to 10 and read at cycle 99, an exponential decay of the per-cycle loss gives a median |ln err| of 0.155 and 0.144 on the LG M50 pools (signed −0.13, −0.12) but 0.21 to 0.34 elsewhere; a linear state feedback dL/dn = a + cL gives the same on LG M50. A charge-throughput feedback (the plating rate scaled by the cycle's charge capacity, Q(L) fitted linearly to cycles 1 to 10, combined with or without 5x's OCP factor, power law on the transformed loss) is badly wrong there: −0.74 and −0.79 signed, and 0.12 to 0.23 worse than 5y on Ai2020. The per-cycle loss divided by the cycle's charge falls by half from cycle 2 to 99 on LG M50, so throughput is at most a part. A 3-cycle smoke run on Chen2020@1.5x design 0 shows the separator-node intercalation overpotential shrinking by about 0.4 mV per cycle at end of charge while the surface OCP moves 0.05 mV.
  • Bench, fixed now (experiments/mechanism/run.py): DFN (SEI solvent-diffusion limited + irreversible plating, as every 100-cycle milestone) to cycle 100 on committed designs, one fresh process per run: 12 from each LG M50 pool of 5w (Chen2020@1.5x, OKane2022@1.5x) and controls, 8 from 5w's NCA_Kim2011@0.875x (where 5x works) and 8 from 5v's Ai2020@0.45x (where it half-works); design indices drawn with random.Random(18) from 0 to 63. Recorded per cycle: lithium lost to SEI and to plating, the charge time, and at the separator-side node of the negative electrode at end of charge the surface potential difference Δφ, the surface open-circuit potential U, the intercalation overpotential η<sub>int</sub> = Δφ − U, the SEI film overpotential η<sub>SEI</sub> and c<sub>e</sub>; and a rate index ∫ c<sub>e</sub> exp(−κ(Δφ + η<sub>SEI</sub>)) dt over the charge at that node (PyBaMM's irreversible plating current, j0 ∝ c<sub>e</sub>, κ = αF/RT = 25.3 V<sup>−1</sup>, α = 0.65 from OKane2022).
  • H139 (plating, not SEI): plating is at least 90% of the lithium lost by cycle 99 on every LG M50 design. Refuted if under 75% on either pool's median. (5p found SEI negligible over 20 cycles; 100 cycles of √t SEI could change that, and SEI would be a self-limiting term of its own.)
  • H140 (a one-node summary is enough): median |ln(index<sub>99</sub>/index<sub>2</sub>) − ln(ΔP<sub>99</sub>/ΔP<sub>2</sub>)| at most 0.20 on both LG M50 pools, ΔP the per-cycle plating loss. Refuted above 0.40 on either.
  • H141 (the mechanism differs by set): the surface-OCP term −κΔU is under half of the end-of-charge exponent change (OCP + η<sub>int</sub> + film + ln c<sub>e</sub> terms) on both LG M50 pools and over half on NCA_Kim2011. Refuted if over half on both LG M50 pools or under half on NCA_Kim2011.
  • H142 (reproduction): each re-run's cycle-99 lithium loss is within 1% of the committed run of the same design. Refuted above 5% on any.
  • Caveats fixed now: 40 designs, all seen at the aggregate level; end-of-charge values at one node summarise a profile in x and t; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only. This milestone names a mechanism; it does not yet give a predictor.
  • Script: experiments/mechanism/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5y outcome: on three fresh pools the plating feedback, with no constant fitted, gets the 100-cycle lithium loss to within 2.4% and 3.8% on NCA_Kim2011 and 10.2% on Ai2020 (the uncorrected ten-cycle law: 31%, 30%, 18%), and one law (a power law on R) replaces 5x's per-pool choice. But on Ai2020 the smaller error ranks worse than 5x's larger, uniform one, and on NCA_Kim2011 raw cycle-10 energy still ranks best. H135, H137, H138 supported; H136 mixed

  • Bench: 192 DFN runs (SEI + plating) to cycle 100, Sobol seed 17, 2 workers, about 55 minutes on 4 cores; no solver drops and no memory kills, so 64 designs per pool (8 calibration, 56 held out for ranks). The report was run once, after the bench finished; experiments/rlaw/run.py was not changed after the plan.
  • H135 supported: median |ln(L_R(99) / L_DFN(99))| 0.102, 0.038, 0.024 on Ai2020@0.55x, NCA_Kim2011@0.75x, @1x, below the uncorrected law's 0.178, 0.297, 0.311 on all three (sign p = 0.25).
  • H136 mixed: at most 0.10 on 2 of 3; Ai2020@0.55x is 0.102 (signed +0.102, an over-prediction, as on all six dev pools), above the bar and below the 0.15 refutation line.
  • H137 supported: its map ranks the held-out DFN@100 Wh/kg at 0.875, 0.819, 0.933, above 5n's √cycle energy fit (0.739, −0.080, −0.561) on all three, and above the one-constant map calibrated on 8 hundred-cycle runs on both NCA_Kim2011 pools (0.623, 0.839). On Ai2020 it trails the one-constant map (0.958), as dev predicted.
  • H138 supported: equal to 5x on both NCA_Kim2011 pools (5u's selector picks the power law there, so the two predictors coincide) and better on Ai2020 (0.102 against 0.323; 5x signed −0.323, the double count replicated on a fresh pool).
  • Descriptive (in the plan's table): raw cycle-10 Wh/kg ranks the 100-cycle energy at 0.947, 0.933, 0.958, at or above every fade-aware list on all three pools (best fade-aware: 5x 0.974 on Ai2020, power-on-R 0.819 and 0.933 on NCA_Kim2011); the map fed DFN's own loss ranks at 0.96 on all three. The power-on-R loss itself ranks the true cycle-99 loss at 0.984 to 0.999. Median DFN fade from cycle 10 to 100 is 0.44 on Ai2020@0.55x and 0.32 to 0.34 on NCA_Kim2011; median lost fraction of lithium 0.30 and 0.44 to 0.48.
  • Reading: the fresh NCA_Kim2011 pools confirm 5x out of sample at two currents no milestone ran to cycle 100: the plating law's own exponential, with α and T from the parameter set and nothing fitted, takes a 30% error to 2 to 4% and outranks an 8-run calibration. On Ai2020 the double count goes away when the law on R is the power law, so one rule now serves both sets, but the size gain does not buy ranking: 5x's 32% under-prediction is nearly uniform across designs and the map, which 5v found amplifies how the error varies between designs, ranks better with it (0.974) than with a 10% error that varies (0.875). Size and order are separate targets, and a fade forecast and a design screen should not be scored on one number. On these pools the cycle-10 energy alone already carries the 100-cycle order (5w's limit again), so none of this tests a screen; that needs pools where fade reorders designs after cycle 10.
  • Caveats: three pools on two sets (sign p = 0.25); the law form was chosen on the ten seen pools; LG M50 sets left out (dev: R carries no feedback there and the power law over-predicts by 35%); SEI treated as plating; open-circuit x1; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/rlaw/bench.jsonl, balance.jsonl, ocp.json, results.txt, summary.json, rlaw.svg; tests tests/test_rlaw.py.

2026-11-15 · Milestone 5y: with the plating feedback taken out, does one law (a power law fitted to R over cycles 2 to 10, on every pool) predict the 100-cycle lithium loss on fresh pools with no constant fitted and no per-pool law choice? (plan, written before any fresh run; H135 to H138 are this entry's)

  • Question: 5x's parameter-free correction fixed NCA_Kim2011 (power law) but double-counted on Ai2020, where 5u's selector picks a + b√n, a curve that already bends like the feedback. Its next step asks for a fit with the feedback present from cycle 1. R is that quantity: if the plating feedback is the only reason the loss decelerates, R should follow a feedback-free law whose shape does not need choosing per pool.
  • Dev, seen (python experiments/rlaw/run.py dev, stdlib, the ten committed 100-cycle pools; three forms were tried on R: linear, a + b√n and a n<sup>b</sup>, so this is a choice made on seen data): the power law on R gives a median |ln(L / L_DFN)| at cycle 99 of 0.080 to 0.105 on the six Ai2020 pools (signed +0.08 to +0.105; 5x 0.30 to 0.32; uncorrected law 0.11 to 0.18), 0.056 and 0.031 on NCA_Kim2011 (equal to 5x, which already used the power law there), and 0.35 to 0.36 on Chen2020 / OKane2022 (law 0.33, 0.34; over-predicting by 35%, where both laws on L under-predict). Linear R: 0.18 to 0.21 on Ai2020; √n R is 5x. On ranks the gain does not follow: the power-on-R map ranks held-out DFN@100 Wh/kg at 0.78 to 0.86 on Ai2020 (5x 0.80 to 0.98, one-constant map 0.89 to 0.98, sqrt fit 0.58 to 0.72) and 0.69, 0.91 on NCA_Kim2011 (one-constant 0.51, 0.76). So on Ai2020 a smaller median error ranks worse than 5x's larger one, which is uniform in sign; the map is sensitive to how the error varies across designs, not to its median (5v's conditioning result).
  • Predictor, fixed now (experiments/rlaw/run.py): per design, 5x's R(L) table (κ = 25.3 V<sup>−1</sup>, the open-circuit upper cut-off, the set's committed OCP), the power law a n<sup>b</sup> fitted to R over cycles 2 to 10, read at cycle 99, inverted to L, fed to 5s's map. No constant is fitted and no law is chosen; every input is the parameter set, the design's balance and its first ten cycles.
  • Fresh pools, fixed now: 64 scrambled Sobol designs (seed 17, used by no milestone; energy-cell bounds) on Ai2020@0.55x (a current no milestone ran to cycle 100), NCA_Kim2011@0.75x and NCA_Kim2011@1x (run to cycle 10 only, on other designs, in 5n), 192 designs. DFN with SEI + plating to cycle 100 with the lithium curve, one fresh process per run, 2 workers. Designs that fail before cycle 100 are dropped and counted. Balance tables were built (no simulation) before this entry.
  • Comparators: the uncorrected pool law (5u), 5x (pool law on R), the one-constant map (5w, 8 calibration designs with random.Random(0)), 5n's √cycle energy fit, raw cycle-10 Wh/kg. Ranks are on 5w's held-out split on every pool.
  • H135 (size, against the law): median |ln(L_R(99) / L_DFN(99))| below the uncorrected law's on all 3 pools. Refuted if on 1 or fewer.
  • H136 (size, absolute): that median at most 0.10 on all 3. Refuted if above 0.15 on any.
  • H137 (ranks): its map ranks the held-out DFN@100 Wh/kg above the sqrt fit on all 3 and within 0.05 of (or above) the one-constant map on both NCA_Kim2011 pools. Refuted if above the sqrt fit on 1 or fewer. Dev expects it to trail the one-constant map on Ai2020, so that pool is reported, not counted, for the second part.
  • H138 (one law, not two): no more than 0.03 worse than 5x on size on all 3 and better than 5x on the Ai2020 pool. Refuted if within 0.03 on 1 or fewer, or not better on Ai2020.
  • Caveats fixed now: three pools on two sets (3 of 3 gives sign-test p = 0.25); the law form was chosen on the ten seen pools; the LG M50 sets are left out because dev says R carries no feedback there (5x) and the power law over-predicts by 35%; lost lithium includes SEI, treated as plating; open-circuit x1; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Script: experiments/rlaw/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5x outcome: the plating law's own exponential, with no constant fitted, gets the 100-cycle lithium loss right on NCA_Kim2011 (median error 5.6% and 3.1%, against the ten-cycle law's 27% and 30%) and orders the cell sets' self-limiting slopes correctly (Spearman 0.92 over ten pools), but it double-counts on Ai2020 (under-predicts the loss by 26 to 28%) and predicts no feedback on the LG M50 sets, whose graphite sits on its plateau at top of charge. H134 supported; H131, H132, H133 refuted

  • Bench: none. Stdlib, 19 s on the ten committed 100-cycle pools (5u, 5v, 5w; 622 designs). The report was run once; experiments/derived/run.py was not changed after it.
  • H131 refuted: the derived loss is closer to DFN than the uncorrected law on 2 of 10 pools, the two NCA_Kim2011 pools (median |ln err| 0.056 and 0.031 against 0.275 and 0.303). On the six Ai2020 pools it is worse (0.30 to 0.32 against 0.11 to 0.18); on Chen2020 and OKane2022 it is the law (0.33, 0.40 against 0.33, 0.34).
  • H132 refuted: at most 0.06 on 2 of 10 (both NCA_Kim2011).
  • H133 refuted on the bar, supported on the order: the derived slope is within 0.15 of the fitted one on 1 of 10 (NCA_Kim2011@0.875x, 0.60 against 0.71; @0.625x 0.63 against 0.81), but the Spearman of derived against fitted slope over the ten pools is 0.915. Derived: 0.29 to 0.33 on Ai2020 (fitted 0.57 to 0.60), 0.02 and −0.01 on Chen2020 / OKane2022 (fitted 0.35, 0.34).
  • H134 supported: on 5w's held-out split the derived map ranks the 100-cycle DFN energy above 5n's √cycle fit on 10 of 10 pools and within 0.05 of the one-constant calibrated map on 8 of 10 (the two misses: Ai2020@0.3x 0.800 against 0.886, @0.35x 0.867 against 0.943). It beats the one-constant map on both NCA_Kim2011 pools (0.692 against 0.514, 0.911 against 0.758) and needs no 100-cycle run.
  • Descriptive (in the plan's table): the median rise of the negative electrode's open-circuit potential at top of charge by cycle 99 is 38 to 42 mV on Ai2020, 132 to 161 mV on NCA_Kim2011, 0.5 mV on Chen2020 and 8.9 mV on OKane2022, so the feedback factor exp(−κΔU) is about 0.36, 0.02 to 0.04 and 0.99 to 0.80.
  • Post hoc (after the verdicts, read off summary.json): the signed median ln(L / L_DFN) is −0.30 to −0.32 derived against −0.10 to +0.05 for the law on Ai2020, so there the √n law fitted to cycles 2 to 10 already carries most of the feedback in its curvature and the derivation applies it twice; on NCA_Kim2011 the power law over-predicts (+0.28, +0.30) and the derivation removes it (−0.06, −0.03); on Chen2020 / OKane2022 both under-predict by about 30% (5t's finding), so what slows loss there is not this term, and the loss is larger than either law says.
  • Reading: the self-limiting correction is, on NCA_Kim2011, PyBaMM's plating exponential acting through the negative electrode's OCP rise at top of charge: a parameter-free prediction fixes a 30% error and outranks a calibration that costs 8 hundred-cycle runs. On Ai2020 the mechanism has the right sign and order (slope 0.3 against 0.6) but the law already absorbs part of it, so the next step is to fit the law to R with the feedback present from cycle 1 (a joint fit, not a transform after a free curvature), or to let the law's exponent be fixed by the set. On the LG M50 sets the plateau leaves no OCP lever, and the fitted slope there (0.35) needs another mechanism (the positive electrode's top-of-charge shift, or SEI); that is now a testable claim, not a calibration.
  • Caveats: ten pools, all seen at the aggregate level (their fitted slopes were in 5v and 5w); lost lithium includes SEI growth, treated as plating; open-circuit x1 at the cut-off, no charge overpotential; OKane2022's plating parameters on every set (5p); one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/derived/results.txt, summary.json, derived.svg; tests tests/test_derived.py (closed form on linear OCPs, recovery of a self-limited power law, no-feedback limit).

2026-11-15 · Milestone 5x: can the correction's slope be derived instead of fitted? The plating law's own exponential with the negative electrode's OCP rise at top of charge, no constant fitted, on the ten committed 100-cycle pools (plan, written before the derived predictor was computed on any design; H131 to H134 are this entry's)

  • Question: 5w found the self-limiting slope S is cell-specific (pooled fits 0.34 to 0.37 on Chen2020 / OKane2022, 0.58 on Ai2020, 0.71 to 0.90 on NCA_Kim2011) and asked for a derivation with those values as its test. A practitioner with a new cell would then need no 100-cycle calibration runs for the slope.
  • Mechanism, fixed now: PyBaMM 26.10.1.1's irreversible plating current is j0 exp(−α F (Δφ + η_SEI) / RT) with α = 0.65 (OKane2022's lithium plating transfer coefficient, used on every set since 5b) and T = 298.15 K (every set's ambient). Lost lithium lowers the negative electrode's stoichiometry at the upper cut-off, x1(n_Li − L) < x1(n_Li), so its open-circuit potential at the end of charge rises by ΔU(L) = U_n(x1(n_Li − L)) − U_n(x1(n_Li)), and to first order Δφ rises with it. So dL/dn = r(n) exp(−κ ΔU(L)), κ = αF/RT = 25.3 V<sup>−1</sup>. With R = ∫<sub>0</sub><sup>L</sup> exp(κ ΔU(l)) dl, dR/dn = r(n): R is the loss the cell would have had without the feedback, which the pool's law (5u's choice) should extrapolate, and L(99) follows by inverting R.
  • Predictor, fixed now (experiments/derived/run.py, stdlib): per design, map each end-of-cycle loss of cycles 2 to 10 to R through the design's own balance (x1 from 5r's window at the open-circuit upper cut-off, U_n from the set's committed OCP table), fit the pool's law to R, read R at cycle 99, invert to L_der(99), and feed 5s's map unchanged. Nothing is fitted to any 100-cycle number; every input is the parameter set, the design's balance and its first ten cycles.
  • Pools: the ten committed 100-cycle pools, all seen (their pooled S values are in 5v and 5w): 5u Ai2020 0.3×, 0.4×, 0.5×, NCA_Kim2011@0.625x; 5v Ai2020 0.35×, 0.45×, 0.6×; 5w NCA_Kim2011@0.875x, Chen2020@1.5x, OKane2022@1.5x. The per-design derived losses have not been computed before this entry. Ranks against the one-constant map are on 5w's held-out designs (8 calibration designs drawn with random.Random(0)) on every pool; the other metrics use every design.
  • H131 (size, against the law): median |ln(L_der(99) / L_DFN(99))| below the uncorrected law's on all 10 pools. Refuted if on 7 or fewer.
  • H132 (size, absolute): that median at most 0.06 on at least 7 of 10 pools. Refuted if on 3 or fewer.
  • H133 (the slope): the derived correction's implied slope (ln(L_law / L_der) = A + S ln(L_law / n_Li) fitted per pool) within 0.15 of the slope fitted to the DFN truth on at least 7 of 10 pools, and Spearman of the two over the 10 pools at least 0.6. Refuted if within 0.15 on 3 or fewer.
  • H134 (ranks): the derived map ranks the held-out DFN@100 Wh/kg above 5n's √cycle energy fit on at least 8 of 10 pools and within 0.05 of (or above) the one-constant calibrated map on at least 7 of 10. Refuted if above the sqrt fit on 5 or fewer.
  • Caveats fixed now: all ten pools were seen at the aggregate level, so this is a test of a parameter-free mechanism against known pools, not a fresh-pool test; the lost lithium also includes SEI growth, which the feedback does not slow in this form (it is treated as plating); the open-circuit x1 ignores the charge overpotential at the cut-off; plating parameters are OKane2022's on every set (5p); one PyBaMM version; modelled fade only.
  • Script: experiments/derived/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5w outcome: the corrected map's ranking carries to three other cell sets with one constant recalibrated on 8 designs (held-out Spearman 0.76, 0.94, 0.94 against the √cycle fit's −0.42, 0.80, 0.80), but the slope does not: Chen2020 and OKane2022 want about 0.36, not Ai2020's 0.577, so the loss size misses the 0.06 bar there (0.087, 0.085). H126, H128, H129 supported; H127, H130 mixed

  • Bench: 192 DFN runs (SEI + plating) to cycle 100, Sobol seed 16, 2 workers, about 33 minutes on 4 cores; no solver drops and no memory kills, so 64 designs per pool, 8 to calibrate and 56 held out. The report was run once, after the bench finished.
  • H126 supported: held-out Spearman(one-constant map, DFN@100 Wh/kg) 0.758, 0.939, 0.936 on NCA_Kim2011@0.875x, Chen2020@1.5x, OKane2022@1.5x, above the sqrt fit's −0.420, 0.796, 0.801 on all three (sign p = 0.25). Over 50 calibration draws it beats the sqrt fit in 50, 50 and 49 of 50 (worst draw 0.672, 0.923, 0.923).
  • H127 mixed: median |ln(L_corr(99) / L_DFN(99))| 0.052, 0.087, 0.085 (bar 0.06; refuted above 0.10). The intercept closes most of the frozen constants' error (0.084, 0.232, 0.253) but not all of it on the NMC811 sets.
  • H128 supported: with 5v's frozen Ai2020 constants that error is above 0.06 on all three pools. Yet the frozen map ranks almost as well as the recalibrated one (0.804, 0.935, 0.932): on these pools a common size error moves every design's loss together and leaves the order nearly intact, where on Ai2020 (5v) it did not.
  • H129 supported, and weak: the union of raw top 4 and one-constant top 4 found the held-out DFN best on all three (gap 0), but so did the raw top 4 alone. The best design is ranked 3rd, 1st and 1st by raw cycle-10 Wh/kg, so these pools do not test the fade list as a screen (the same limit 5t disclosed for its Chen2020, NCA_Kim2011 and OKane2022 pools).
  • H130 mixed: the one-constant map ranks at least as well as the two-constant refit on 2 of 3 (Chen2020 0.939 against 0.919, OKane2022 0.936 against 0.917; NCA_Kim2011 0.758 against 0.813). Over 50 draws its worst case is better on all three (0.672, 0.923, 0.923 against 0.625, 0.851, 0.859).
  • Descriptive (in the plan): the pool's in-sample slope S is 0.709 (NCA_Kim2011), 0.349 (Chen2020) and 0.339 (OKane2022), against 0.577 on Ai2020. Raw cycle-10 Wh/kg ranks the 100-cycle energy at 0.959, 0.932 and 0.927, above every fade list on NCA_Kim2011 and within 0.01 of the one-constant map on the other two; the map fed DFN's own loss ranks at 0.964, 0.922 and 0.917. Median DFN fade from cycle 10 to 100 is 0.32 to 0.33 on all three.
  • Post hoc (after the verdicts, /tmp scratch, not committed): the two-constant refit on the same 8 designs brings the held-out lithium error to 0.069, 0.026 and 0.026, with S = 0.90, 0.37 and 0.36. On the NMC811 sets the ratio L_law / L_DFN rises with the true lost fraction as on Ai2020 (Spearman 0.88, 0.89); on NCA_Kim2011 it does not (−0.18), as 5v's dev found (−0.49).
  • Reading: for ranking, the correction is portable: one constant set from 8 designs is enough, the slope from another cell does no harm, and a stable one-constant fit is safer than a two-constant one on 8 points. For the size of the loss, which a fade forecast needs, the slope is set-specific (0.34 to 0.37 on the two LG M50 parameterisations, 0.58 on Ai2020, 0.7 to 0.9 on NCA_Kim2011). That is a reason to derive S from the plating law rather than to fit it, and a test for any derivation: it must give about 0.36 on Chen2020 and OKane2022 and about 0.58 on Ai2020. On these three pools the cycle-10 energy alone already carries the order, so a screen test needs pools where the best design is not near the top at cycle 10 (fade-limited Ai2020 currents, or a slower set).
  • Caveats: three pools, one per set (sign p = 0.25); the screen part is untested here (best design in raw top 3); Chen2020 and OKane2022 are two parameterisations of one cell (LG M50; identical positive-electrode OCP in the tables here, different negative-electrode OCP), not two independent cells; plating parameters are OKane2022's on every set (5p); open-circuit map; one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/crossset/bench.jsonl, balance.jsonl, ocp.json, results.txt, summary.json, crossset.svg.

2026-11-15 · Milestone 5w: does 5v's self-limiting correction carry to other chemistries when only its intercept is recalibrated, on 8 designs per pool, with the slope kept from Ai2020? (plan, written before any fresh run; H126 to H130 are this entry's)

  • Question: 5v's corrected map beat 5n's √cycle energy fit on three fresh Ai2020 pools with A = 0.658, S = 0.577 frozen, but on the set the constants came from. Its next step asks whether the correction carries to NCA_Kim2011, Chen2020 and OKane2022 with constants self-calibrated on 8 designs. A practitioner with a new cell needs to know how many 100-cycle runs that costs and which constant must move.
  • Dev, seen (python experiments/crossset/run.py dev, stdlib, 50 random draws of 8 calibration designs on each committed 5u and 5v pool, ranks on the 45 to 56 held-out designs): refitting both A and S on 8 designs is unstable, with S from −0.42 to 2.08 on 5u's NCA_Kim2011@0.625x pool (held-out map rank median 0.616, worst −0.081) and 0.39 to 0.82 on the six Ai2020 pools (worst 0.78 to 0.90). Refitting only A with S held at 0.577 gives held-out medians 0.922 to 0.974 on Ai2020 (worst 0.875) and 0.537 on NCA_Kim2011 (worst 0.475), against the √cycle fit's 0.59 to 0.75 and −0.15. On NCA_Kim2011 raw cycle-10 Wh/kg ranks at 0.914, above any fade list. On the 5s diagnostic designs (8 Chen2020@0.5x, 6 OKane2022@1x; too few to split) the frozen Ai2020 constants leave a median |ln error| of 0.054 and 0.128 on the cycle-99 lithium loss, and the in-sample slopes are 0.47 and 0.38.
  • Predictor, fixed now (experiments/crossset/run.py): per pool, 5u's law choice and the cycle-99 law loss as in 5v; 8 completed designs drawn with random.Random(0) are run to cycle 100 and set A = mean of ln(L_law / L_DFN) − 0.577 ln(L_law / n_Li); then L_corr and 5s's map as in 5v. Everything is scored on the other designs only (held out).
  • Fresh pools, fixed now: 64 scrambled Sobol designs (seed 16, used by no milestone; energy-cell bounds) on NCA_Kim2011@0.875x, Chen2020@1.5x and OKane2022@1.5x, 192 designs; DFN with SEI + plating to cycle 100 with the lithium curve, one fresh process per run, 2 workers. Designs that fail before cycle 100 are dropped and counted. Balance tables were built (no simulation) before this entry.
  • Comparators: 5n's sqrt energy fit and union (raw top 4 plus sqrt top 4), 5v's frozen map, the two-constant refit on the same 8 designs, raw cycle-10 Wh/kg.
  • H126 (ranks): Spearman(one-constant map, DFN@100 Wh/kg) on held-out designs above the sqrt fit's on all 3 pools. Refuted if on 1 or fewer.
  • H127 (lithium size): median |ln(L_corr(99) / L_DFN(99))| at most 0.06 on every pool. Refuted if above 0.10 on any.
  • H128 (the intercept must move): with 5v's frozen Ai2020 constants the same error exceeds 0.06 on at least 2 of 3 pools. Refuted if at most 0.06 on all 3.
  • H129 (screen): the union of raw top 4 and one-constant top 4 within 0.5% of the held-out pool's DFN best on every pool. Refuted if above 2% on any.
  • H130 (one constant is enough): the one-constant map ranks at least as well as the two-constant refit on all 3. Refuted if on 1 or fewer.
  • Reported beside, not counted: the same metrics over 50 calibration draws (median and worst), the pool's in-sample slope, the map fed DFN's own loss.
  • Caveats fixed now: three pools, one per set (3 of 3 gives sign-test p = 0.25); the slope is still fitted, not derived; plating parameters are OKane2022's on every set (5p); open-circuit map, which 5t found under-predicts fade on the NMC811 sets; one PyBaMM version (26.10.1.1); the calibration designs cost 8 extra 100-cycle runs per new pool, on top of the union's resumed designs.
  • Script: experiments/crossset/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5v outcome: the map's failure was conditioning, and one self-limiting correction fixes it out of sample. With A = 0.658, S = 0.577 frozen from 5u's pools, the corrected map ranks the 100-cycle DFN energy at 0.92, 0.96 and 0.96 on three fresh Ai2020 pools (5n's √cycle energy fit 0.59 to 0.67, 5u's uncorrected map 0.61 to 0.82) and gets the cycle-99 lithium loss to a median 4% (uncorrected 11 to 18%). H122, H123, H124 supported, H125 mixed

  • Bench: 192 DFN runs (SEI + plating) to cycle 100, Sobol seed 15, 2 workers, about 54 minutes on 4 cores; no memory kills. 3 designs dropped by the solver (IDA failures, 2 on Ai2020@0.35x, 1 on @0.45x), so 62, 63 and 64 were scored. The report was run once, after the bench finished.
  • H122 supported: Spearman(corrected map, DFN@100 Wh/kg) 0.918, 0.955, 0.963 on Ai2020 0.35×, 0.45×, 0.6×, above the sqrt fit's 0.670, 0.618, 0.590 on all three (sign test p = 0.25 at n = 3) and within 0.01 to 0.04 of the map fed DFN's own loss (0.961, 0.963, 0.969). The uncorrected 5u map ranks at 0.610, 0.681, 0.816.
  • H123 supported: median |ln(L_corr(99) / L_DFN(99))| 0.039, 0.036, 0.040 (bar 0.06); uncorrected 0.112, 0.158, 0.182.
  • H124 supported: the union of raw top 4 and corrected-map top 4 found the pool's DFN best on all three (gap 0), as did 5n's union, at 6.3 resumed designs on average against 7.7.
  • H125 mixed: a 10% lognormal error on the true loss lowers the map's Spearman by 0.52, 0.37 and 0.19 (bar 0.2 on every pool; refuted below 0.1). The map is ill-conditioned at low current and less so at 0.6×, where the fade is smaller (median 0.43 against 0.50).
  • Descriptive (in the plan, not counted): the uncorrected law ranks the cycle-99 lithium loss itself at 0.989, 0.976, 0.970 (corrected 0.993, 0.990, 0.989), so the order of the loss was never the problem; its error ratio rises with the true lost fraction (Spearman 0.89, 0.86, 0.79), as on dev. Refitted on 8 random designs per pool run to cycle 100 the constants are A = 0.61 to 0.72, S = 0.57 to 0.60 (frozen 0.658, 0.577) and the self-calibrated map ranks at 0.934, 0.947, 0.961: a user calibrating on a new pool loses nothing measurable here.
  • Not in the plan, read off the same table: raw cycle-10 Wh/kg alone ranks the 100-cycle energy at 0.534, 0.884 and 0.976, above the corrected map on Ai2020@0.6x (0.963). As fade shrinks with current, the cycle-10 energy carries the order and any fade list matters less; the correction matters where fade decides (0.35×: 0.918 against 0.534).
  • Reading: 5u's diagnosis was half right. The per-design extrapolation was the problem, but not its ranking: the map amplifies a size error (a 10% random error costs 0.2 to 0.5 of Spearman), and the ten-cycle law's size error is systematic, larger for designs that lose more, as a self-limiting loss would be. A two-constant line in log space removes it, and constants fitted on one set of three pools carry to three fresh pools of the same set, two at currents no milestone ran. The map with this correction is the first ten-cycle fade predictor in the programme to beat 5n's energy fit out of sample on every pool; 5n's union now has a cheaper equal (6.3 designs resumed, not 7.7).
  • Caveats: three pools of one set, the set the constants came from; NCA_Kim2011 needs its own slope (0.81 on dev) and Chen2020 / OKane2022 are untested; the correction is empirical, with no mechanism fitted (the slope 0.58 is not derived); plating parameters are OKane2022's (5p); open-circuit map; one PyBaMM version (26.10.1.1); modelled fade only.
  • Output: experiments/calmap/bench.jsonl, balance.jsonl, ocp.json, results.txt, summary.json, calmap.svg.

2026-11-15 · Milestone 5v: is the balance map's ranking failure a conditioning problem, and does one self-limiting correction of the ten-cycle lithium law, fitted on 5u's Ai2020 pools and frozen, carry to fresh Ai2020 pools? (plan, written before any fresh run; H122 to H125 are this entry's)

  • Question: 5u's reading was that the per-design ten-cycle law gets the cycle-99 lithium loss wrong and the next predictor "should be judged on the lithium Spearman first". Dev on 5u's committed pools (seen; python experiments/calmap/run.py dev, stdlib) says that is the wrong target: the √n / power law already ranks the cycle-99 DFN lithium loss at Spearman 0.98 to 0.99 on all four pools (the cycle-10 loss alone ranks it at 0.98 to 0.998). The map is ill-conditioned: fed the true loss times exp(N(0, 0.1)) it ranks the 100-cycle energy at 0.38, 0.54, 0.67 and 0.48 (mean of 20 draws) against 0.95 to 0.97 with the exact loss, and a uniform 1.25× over-prediction alone drops it to 0.65 to 0.74. So what decides the ranking is the per-design size of the loss to within a few percent, not its order.
  • Dev, seen: the law's error is systematic, not noise. L_law(99) / L_DFN(99) rises with the predicted fraction of lithium lost (Spearman with the true fraction 0.93, 0.88, 0.82 on Ai2020 0.3×, 0.4×, 0.5×; −0.49 on NCA_Kim2011@0.625x): designs that lose more slow down more. One line, ln(L_law / L_DFN) = A + S ln(L_law / n_Li), fitted pooled on the three Ai2020 pools gives A = 0.658, S = 0.577 (per-pool slopes 0.57, 0.60, 0.59). In sample it cuts the median |ln error| from 0.12 to 0.18 down to 0.026 to 0.038 and lifts the map's energy ranking from 0.64 to 0.76 to 0.90, 0.97 and 0.97 (true-loss map 0.97, 0.97, 0.96). On NCA_Kim2011 the slope is 0.81 and the pooled Ai2020 constants give 0.58; the correction is a per-set calibration, and this milestone tests it on Ai2020 only. Also seen: refitting the law to cycles 2 to 20 (a cycle-20 rung, 5u's other suggestion) narrows the ratio spread a little but ranks the energy worse (0.60 to 0.71 on Ai2020), so it is not taken further. 5u's first suggestion, one curvature per pool (the law fitted to the pool's median normalised curve) with a per-design scale (the cycle-10 loss, or a least-squares scale over cycles 2 to 10), ranks the energy at 0.62 to 0.75 on Ai2020 and 0.37 to 0.40 on NCA_Kim2011, no better than the per-design law, because it keeps the same size error. Nothing beyond these numbers was computed before this entry (the dev scripts are in experiments/calmap/run.py dev for the correction; the curvature and cycle-20 checks were scratch and are not committed).
  • Predictor, fixed now (experiments/calmap/run.py): 5u's per-pool law (median ten-cycle exponent ≥ 0.6 takes a + b√n, else a n<sup>b</sup>), read at cycle 99, then L_corr = L_law / exp(0.658 + 0.577 ln(L_law / n_Li)), then 5s's map unchanged (cycle-10 Wh/kg × E_ocv(n_Li − L_corr) / E_ocv(n_Li − lost by end of cycle 9), floored at the cycle-9 loss). Only cycles 1 to 10 of each design are read; A and S are frozen.
  • Fresh pools, fixed now: 64 scrambled Sobol designs (seed 15, used by no milestone; energy-cell bounds) on Ai2020@0.35x (a current 5s ran, new designs), Ai2020@0.45x and Ai2020@0.6x (currents no milestone ran), 192 designs. DFN with SEI + plating to cycle 100 with the lithium curve, one fresh process per run, 2 workers (5u: three ran out of 15 GB). Designs that fail before cycle 100 are dropped and counted.
  • Comparators: 5n's sqrt energy fit (cycles 5 to 10, read at 100), 5n's union (raw top 4 plus sqrt top 4), 5u's uncorrected map.
  • H122 (ranks): Spearman(corrected map, DFN@100 Wh/kg) above the sqrt fit's on all 3 pools and at least 0.85 on each. Refuted if below the sqrt fit on 2 or more, or below 0.75 on any.
  • H123 (lithium size): median |ln(L_corr(99) / L_DFN(99))| at most 0.06 on every pool. Refuted if above 0.10 on any.
  • H124 (screen): the union of raw top 4 and corrected-map top 4 within 0.5% of the pool's DFN best and no more than 0.5 points worse than 5n's union on every pool. Refuted if above 2% on any.
  • H125 (conditioning, replicated): a 10% lognormal error on the true cycle-99 loss lowers the map's Spearman by at least 0.2 on every pool (mean of 20 draws). Refuted if by less than 0.1 on any.
  • Reported beside, not counted: a self-calibrated variant (A, S refitted on 8 random designs of the same pool run to cycle 100, the cost a user would pay on a new cell set), the uncorrected map, the true-loss map, the lithium Spearman of each.
  • Caveats fixed now: three pools (3 of 3 gives sign-test p = 0.25); one set (Ai2020), the set the constants came from; the correction is empirical, a line in log space with no mechanism fitted; plating parameters are OKane2022's (5p); open-circuit map; one PyBaMM version (26.10.1.1).
  • Script: experiments/calmap/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5u outcome: on four fresh pools (256 unseen designs) the per-pool law choice works and the √n law gets the median cycle-99 lithium loss right out of sample (0.94 to 1.05 on Ai2020), but the map still ranks the 100-cycle DFN energy worse than 5n's √cycle energy fit on 3 of 4 pools. Fed DFN's own loss the same map ranks at 0.95 to 0.97 on all four, so what is left is the per-design lithium extrapolation (10th to 90th percentile 0.77 to 1.45 of the truth). H121 supported, H118 mixed, H117, H119 and H120 refuted. 5n's union stays the procedure

  • Bench: 256 DFN runs (SEI + plating) to cycle 100, Sobol seed 14, about 90 minutes on 4 cores. Three workers ran out of memory (two runs killed by the kernel, exit −9; amended before any result was read: 2 workers, killed runs retried, the predictor untouched). 15 designs dropped by the solver (IDA failures, 11 on Ai2020@0.3x, 4 on Ai2020@0.4x, the same first-cycle failures 5l and 5n saw below 0.4×), so 53, 60, 64 and 64 designs were scored. The report code was run once on the finished Ai2020@0.3x pool with its output discarded, to check it ran, before the other pools finished.
  • H121 supported: the selector picked √n on the three Ai2020 pools (b_med 0.86, 0.88, 0.90) and the power law on NCA_Kim2011@0.625x (b_med 0.25), as 5s's pools predicted. Median L_law(99) / L_DFN(99): 1.05, 0.99 and 0.94 on Ai2020 0.3×, 0.4×, 0.5× (bar 0.8 to 1.25), 1.32 on NCA_Kim2011 with the power law (5t's √n law was 1.66 there on dev). The law is right on the median on designs nobody had looked at.
  • H117 refuted: Spearman(map, DFN@100) above the sqrt fit's on 1 of 4 (Ai2020@0.5x, 0.764 against 0.666). Ai2020@0.3x 0.641 against 0.667, @0.4x 0.662 against 0.745, NCA_Kim2011@0.625x −0.352 against −0.157 (both below the raw cycle-10 energy's 0.914 there).
  • H118 mixed, H119 refuted: the union of raw top 4 and map top 4 found the DFN best on three pools and missed by 1.25% on Ai2020@0.4x, where the best ranks 22nd by the map and 1st by the sqrt fit; 5n's union is exact there and misses by 0.87% on Ai2020@0.5x (where the map's union is exact). Excess over 5n's union: +1.25 points at worst (bar 1).
  • H120 refuted: median |fade error| from cycle 10 to 100 below the sqrt fit's on 1 of 4 (NCA_Kim2011, 0.40 against 0.70); 0.080, 0.103 and 0.123 against 0.075, 0.079 and 0.107 on Ai2020.
  • Descriptive (in the plan, not counted): fed DFN's own cycle-99 lithium loss the map ranks the 100-cycle energy at 0.974, 0.968, 0.961 and 0.952, with median fade error 0.016 to 0.033 on all four pools, including NCA_Kim2011, where every energy extrapolation ranks negatively. 5s's decomposition, checked on 27 designs, holds on 241 unseen ones. The law the selector did not pick ranks worse on every pool (0.28 to 0.43 on Ai2020 with the power law; −0.49 on NCA_Kim2011 with √n). The three-list union (raw + sqrt + map, 4 each) is exact on all four pools at 11.0 resumed designs against 7.8 for 5n's; the top 8 by raw cycle-10 energy alone misses by 2.74% and 1.44% on Ai2020 0.3× and 0.4×.
  • Post hoc (after the verdicts): the per-design ratio L_law(99) / L_DFN(99) runs from 0.77 to 0.89 at the 10th percentile to 1.28 to 1.45 at the 90th on Ai2020 (1.19 to 1.50 on NCA_Kim2011). Getting the pool median right is not enough: this per-design spread is what separates the map's 0.64 to 0.76 from its 0.95 to 0.97 when fed the true loss.
  • Reading: the decomposition is right and now tested out of sample: energy fade at cycle 100 is the electrode-balance map of the lithium lost (Spearman 0.95 to 0.97 on four fresh pools). The pool-level law choice from the ten-cycle exponent works. What fails is ranking designs by a two-parameter law fitted per design to cycles 2 to 10: the curvature that decides the late loss is not identifiable from ten cycles for each design. The next predictor should share information across a pool (one curvature per pool, fitted to the median curve, with a per-design scale) or read one later rung (cycle 20) where the deceleration has begun, and should be judged on the lithium Spearman first, since the map turns a good lithium ranking into a good energy ranking.
  • Caveats: four pools (4 of 4 would give sign-test p = 0.125); one Sobol pool per condition; 15 solver drops on the two lowest-current pools; plating parameters are OKane2022's on both sets (5p); open-circuit map; one PyBaMM version (26.10.1.1); Chen2020 and OKane2022 not tested.
  • Output: experiments/freshlaw/bench.jsonl, balance.jsonl, ocp.json, results.txt, summary.json, freshlaw.svg.

2026-11-15 · Milestone 5u: on fresh pools nobody has seen, does the balance map with a lithium-loss law chosen per pool from the ten-cycle curve rank the 100-cycle DFN energy and carry the union screen? (plan, written before any run; H117 to H121 are this entry's)

  • Question: 5t's √n law ranked better than 5s's power law on 12 of 13 committed pools, but it was chosen on 27 designs of the same family, scored against truth read since 5b, and over-predicted NCA_Kim2011's decelerating loss. Both open items in 5t's next step meet here: choose the law from the curve itself, and test on pools where neither truth nor lithium curve has been seen.
  • Predictor, fixed now (experiments/freshlaw/run.py): per pool, b_med = median over designs of 5s's power-law exponent of the lithium lost by the end of cycles 2 to 10. b_med ≥ 0.6 takes L(n) = a + b√n (5t), b_med < 0.6 the power law a n<sup>b</sup> (5s). On 5s's 17 pools b_med was 0.84 to 0.96 on every graphite pool and 0.23 to 0.30 on NCA_Kim2011; 0.6 sits in that gap and nothing was tuned on fade or energy. Then 5s's map unchanged: predicted cycle-100 Wh/kg = cycle-10 Wh/kg × E_ocv(n_Li − L(99)) / E_ocv(n_Li − lost by end of cycle 9), L(99) floored at the cycle-9 loss.
  • Fresh pools, fixed now: 64 scrambled Sobol designs (seed 14, used by no milestone; energy-cell bounds) on Ai2020@0.3x, Ai2020@0.4x (a current no milestone ran), Ai2020@0.5x and NCA_Kim2011@0.625x (a current no milestone ran), 256 designs. DFN with SEI + plating (5r's both) to cycle 100 with the lithium curve, one fresh process per run, 3 workers (four ran out of memory in 5s's diagnostic). The screen reads cycles 1 to 10 of the same run; 5s showed a separate ten-cycle run reproduces them exactly. Designs that fail before cycle 100 are dropped and counted.
  • Comparators: 5n's sqrt energy fit (cycles 5 to 10, read at 100) and 5n's union (raw top 4 plus sqrt top 4).
  • H117 (ranks): Spearman(map, DFN@100 Wh/kg) above the sqrt fit's on at least 3 of 4 pools. Refuted if on 2 or fewer.
  • H118 (screen): the union of raw top 4 and map top 4 within 1% of the pool's DFN best on every pool. Refuted if above 3% on any.
  • H119 (against 5n): that union's gap no larger than 5n's union's on every pool. Refuted if larger by more than 1 point on any.
  • H120 (fade size): median |predicted − DFN fade from cycle 10 to 100| below the sqrt fit's on at least 3 of 4. Refuted if on 2 or fewer.
  • H121 (the law out of sample): the selector picks the power law on NCA_Kim2011 and √n on the three Ai2020 pools, and on each Ai2020 pool the median L_law(99) / L_DFN(99) is within 0.8 to 1.25 (5t's dev: 1.04 on Ai2020@0.3x). Refuted if the selector picks otherwise or a ratio is outside 0.67 to 1.5.
  • Reported beside, not counted: the map with the law not picked, the map fed DFN's own cycle-99 loss (5s's decomposition, now on 256 unseen designs), the three-list union, and the top 8 by raw cycle-10 energy (a cost-matched list with no fade model).
  • Caveats fixed now: four pools, so a sign test cannot reach p < 0.05 (4 of 4 gives p = 0.125); one Sobol pool per condition; plating parameters are OKane2022's on Ai2020 and NCA_Kim2011 (5p); the map is open-circuit; one PyBaMM version (26.10.1.1); Chen2020 and OKane2022, where 5r and 5t found a rate effect, are not tested.
  • Script: experiments/freshlaw/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5t outcome: the √n loss law fixes the map's ranking (better than 5s's power law on 12 of 13 test pools, sign test p = 0.003) and ranks the 100-cycle DFN energy better than 5n's √cycle energy fit on 8 of 13, one short of the bar; its fade size is worse on 7 of 13 and, as the union's fade list, it misses by up to 3.2%. H116 supported, H112 mixed, H113 to H115 refuted. 5n's union stays the procedure

  • Bench: none. The report reads 5s's committed ten-cycle DFN runs (bench.jsonl, 1,108), balance tables and the committed 100-cycle pools, and runs in about 2 s with the standard library. 5s's own report regenerates byte for byte from the same files.
  • H112 mixed: Spearman(√n map, DFN@100 Wh/kg) above the sqrt fit's on 8 of 13 test conditions (bar 9; refuted at 6 or fewer; sign test p = 0.58). Wins: Ai2020 0.275×, 0.35×, 0.4375×, 0.5×, 0.625× (0.809 against 0.578), Chen2020 1× and 2× (0.901 against 0.572), OKane2022@2x (0.897 against 0.570). Losses: Ai2020 0.25× (0.605 against 0.647) and 0.375× (0.671 against 0.676), OKane2022@1.25x (0.866 against 0.896) and both NCA_Kim2011 pools (−0.45 and −0.46 against −0.02 and −0.33).
  • H113 refuted: median |fade error| below the sqrt fit's on 6 of 13 (four Ai2020, both NCA_Kim2011, the latter only because both are far off: 0.62 to 0.63 against 0.69). On Chen2020 and OKane2022 the map under-predicts the fade (median 0.08 to 0.21 against DFN's 0.24 to 0.37), the same direction 5r saw over 20 cycles; on NCA_Kim2011 it saturates (0.97 to 0.98 against 0.34 to 0.36), because the law over-predicts that set's decelerating loss (it did by 1.66 on dev).
  • H114 refuted: the union of raw top 4 and √n-map top 4 missed the DFN best by 3.17% on Ai2020@0.275x (the bar is 3%), 2.17% on @0.5x and 1.19% on @0.25x; exact or within 0.08% on the other 10.
  • H115 refuted: worse than 5n's union by up to 3.0 points (Ai2020@0.275x, where 5n's misses by 0.16%).
  • H116 supported: the √n map ranks better than 5s's power-law map on 12 of 13 (p = 0.003); the exception is NCA_Kim2011@0.5x (−0.45 against −0.26). Read at cycle 99 the power law predicts 1.8 to 2.2 times the √n law's loss on the graphite pools and 0.78 to 0.80 of it on NCA_Kim2011.
  • Descriptive, not in the plan (the three-list union, top 4 each by raw, sqrt fit and √n map, written into the script before its first run): within 0.16% on all 13 test pools, the same worst case as 5n's union, at a mean 9.8 resumed designs against 7.4. It buys nothing here.
  • Dev (seen): with the √n law the map's mean fade error on the 27 diagnostic designs is 0.14 (Ai2020@0.3x), 0.07 (Chen2020@0.5x), 0.18 (OKane2022@1x) and 0.61 (NCA_Kim2011@1x), against 0.02 to 0.12 fed DFN's own loss (5s): getting L(99) right on the median is not enough, because the per-design ratio still spreads (0.93 to 1.75 on Ai2020@0.3x) and the map is steep where the window shrinks.
  • Reading: a decelerating loss law is most of what the map was missing as a ranker. On the eight graphite pools where the sqrt fit ranks below 0.70 (Ai2020 0.25× to 0.4375×, 0.625×, Chen2020@2x, OKane2022@2x) the √n map is at 0.61 to 0.90, and by ≥ 0.3 above on the two 2× pools. It is not yet a fade-size predictor (rate effect on NMC811 sets, saturation on NCA) and not a safe fade list on its own (3.2% miss). The useful next step is a per-set law choice made from the curve itself (the power-law exponent over cycles 2 to 10, a pool median of 0.23 to 0.30 on NCA_Kim2011 against 0.84 to 0.96 on the graphite pools in 5s, already separates them), and a test on fresh pools where neither the truth nor the law's dev has been seen.
  • Caveats: committed pools (truth seen since 5b); the law was chosen on 27 designs of four conditions from the same 17-pool family; no new simulation; 9 of the 17 pools came in through 5s's Wh/Wh-per-kg selection slip, so 7 of the 13 test pools (Ai2020@0.625x, both Chen2020, both NCA_Kim2011, both OKane2022) have the DFN best inside the raw top 4 by Wh/kg and test the fade list less; all three union misses are on the other six; one PyBaMM version (26.10.1.1).
  • Output: experiments/losslaw/results.txt, summary.json, losslaw.svg.

2026-11-15 · Milestone 5t: does a √n lithium-loss law, fitted to the same ten DFN cycles, fix 5s's over-prediction well enough for the balance map to be the union screen's fade list? (plan, written before any test condition's prediction under the new law was computed; H112 to H116 are this entry's)

  • Question: 5s found the balance map right (within a mean 0.02 to 0.05 of DFN's 100-cycle fade on three of four diagnostic conditions when fed DFN's own lithium loss) and the power law wrong (cycle-99 loss over-predicted 1.2 to 2.8 times, because plating slows). If a decelerating law fitted to the same cycles 2 to 10 gets cycle-99 loss right, the map becomes a fade list at no new simulation cost: everything needed (1,108 ten-cycle lithium curves, balance tables, committed 100-cycle truth) is already committed.
  • Development, seen before this entry (the 27 designs 5s's post hoc diagnostic ran to cycle 100 with their lithium curves, on Ai2020@0.3x, NCA_Kim2011@1x, Chen2020@0.5x, OKane2022@1x): median predicted / DFN lithium lost by cycle 99, per condition in that order, for six laws fitted to the end-of-cycle loss: power law a n<sup>b</sup> on cycles 2 to 10 (5s) 1.93, 1.36, 1.91, 1.61; the same on cycles 6 to 10 1.74, 1.22, 1.68, 1.52; a quadratic in log-log on cycles 2 to 10 (exponent floored at 0) 1.40, 0.91, 1.29, 1.38; a power law of the per-cycle loss on cycles 3 to 10, summed 1.57, 1.02, 1.50, 1.44; a + b√n on cycles 6 to 10 1.13, 1.47, 1.08, 0.84; a + b√n on cycles 2 to 10 1.04, 1.66, 1.00, 0.75. Chosen on that: the last, the SEI-growth form, nearest 1 on the three graphite conditions. Nothing else from the diagnostic (no fade, rank or screen number under any new law) was computed before this entry.
  • Predictor, fixed now (experiments/losslaw/run.py): L(n) = a + b√n, least squares through the run's "Total lithium lost" at the end of cycles 2 to 10, read at n = 99 and floored at the cycle-9 loss; then 5s's map unchanged: predicted cycle-100 Wh/kg = cycle-10 Wh/kg × E_ocv(n_Li − L(99)) / E_ocv(n_Li − lost by end of cycle 9). No constant fitted to fade or energy; the law's choice is the only thing tuned, on lithium only.
  • Test conditions, fixed now: 5s's 17 minus the four diagnostic ones, 13 conditions, 902 designs (Ai2020 0.25×, 0.275×, 0.35×, 0.375×, 0.4375×, 0.5×, 0.625×; Chen2020 1×, 2×; NCA_Kim2011 0.5×, 0.75×; OKane2022 1.25×, 2×). Their 100-cycle truth was read by 5b to 5s; their lithium beyond cycle 10 has never been simulated. The four diagnostic conditions are reported beside, not counted.
  • Comparators: 5n's sqrt fit of the energy (cycles 5 to 10, read at 100), 5n's union (top 4 raw plus top 4 sqrt), and 5s's power-law map.
  • H112 (ranks): Spearman(√n map, DFN@100 Wh/kg) above the sqrt fit's on at least 9 of 13. Refuted if on 6 or fewer.
  • H113 (fade size): median |predicted − DFN fade from cycle 10 to 100| below the sqrt fit's on at least 9 of 13. Refuted if on 6 or fewer.
  • H114 (screen): the union of the top 4 raw and the top 4 by the √n map is within 1% of the pool's DFN best on every test condition. Refuted if above 3% on any.
  • H115 (against 5n): that union's gap is no larger than 5n's union's on every test condition. Refuted if larger by more than 1 point on any.
  • H116 (the law is the fix): the √n map's Spearman with DFN@100 is above 5s's power-law map's on at least 10 of 13. Refuted if on 6 or fewer.
  • Caveats fixed now: committed pools (truth seen by earlier milestones, predictor unseen); the law was picked on 27 designs from four conditions, and it over-predicts NCA_Kim2011@1x's loss there by 1.66, so NCA_Kim2011 test pools are expected to be its weakest; the map is open-circuit (5r's H107); plating parameters are OKane2022's on six of seven sets; one PyBaMM version (26.10.1.1); no new simulation, so nothing here checks the fresh-run reproducibility that 5s already did.
  • Script: experiments/losslaw/run.py; outcome logged above this entry.

2026-11-15 · Milestone 5s outcome: the balance map is right, the lithium extrapolation is not. A power law through ten DFN cycles' lithium loss over-predicts the cycle-99 loss 1.2 to 2.8 times, so the map's predicted fade ranks 100-cycle DFN worse than 5n's sqrt fit on 15 of 17 conditions and the union with it misses by up to 6.9%. H108 to H111 refuted

  • Bench: 1,108 ten-cycle DFN runs (SEI + plating), 4 workers, about 28 minutes on 4 cores; none failed. Cycle-10 Wh/kg reproduces every committed run exactly (max relative difference 0). The map costs under a millisecond per design once each set's OCP table exists (four sets, 1.6 s in all), so as a fade list it would be free.
  • H108 refuted: Spearman(map prediction, DFN@100) beat the sqrt fit's on 2 of 17 (NCA_Kim2011@1x −0.27 against −0.60, OKane2022@2x 0.63 against 0.57). On Ai2020 0.25× to 0.5× the map ranks at 0.27 to 0.55 against 0.57 to 0.76 for the sqrt fit; on Chen2020@0.5x it is anti-correlated (−0.46).
  • H109 refuted: the map's median |fade error| from cycle 10 to 100 was below the sqrt fit's on 7 of 17, the three NCA_Kim2011 conditions, where the sqrt fit itself fails (0.38 to 0.41 against 0.50 to 0.69), Chen2020@2x and the three OKane2022 pools; on none of the eight Ai2020 pools. On Ai2020 the map predicts a median fade of 0.87 to 0.99 against DFN's 0.45 to 0.56.
  • H110 refuted: the union of the raw top 4 and the map's top 4 missed the pool's DFN best by up to 6.88%, above 3% on three conditions (Ai2020 0.25× 6.88%, 0.275× 3.17%, 0.3× 5.58%).
  • H111 refuted: it was worse than 5n's union on 7 conditions, every Ai2020 pool from 0.25× to 0.5×, by up to 6.88 points. 5n's union (raw top 4 plus sqrt top 4) is exact on 13 of the 17 and within 0.32% on all.
  • Amended after the first report, before this entry: 5m's and 5n's committed pools store Wh/kg with mass 1; the first report divided the fresh runs' Wh by that 1 and so ranked those five pools in Wh. It now divides by each design's stack mass (recorded by tables, pybamm parameter values only), and the reproduction check is in Wh/kg. That moved Ai2020@0.275x, @0.3x, @0.35x and @0.4375x; no verdict changed (H108 was 3 of 17 before, 2 after). The same slip was in the condition rule: it ranked committed cycle-10 energy in Wh, so 9 of the 17 have the DFN best inside the raw top 4 by Wh/kg. On the 8 that meet the rule as meant (seven Ai2020 pools and NCA_Kim2011@1x) the map beats the sqrt fit on ranking on 1 and the union's worst gap is 6.88% against 0.32% for 5n's.
  • Post hoc, why (after the verdicts; diag in the script): DFN to cycle 100 with the lithium curve on the first 8 designs of Ai2020@0.3x, NCA_Kim2011@1x, Chen2020@0.5x and OKane2022@1x, 27 of 32 completed (five were killed for memory with four parallel 100-cycle runs, not by the solver; cycle-100 Wh/kg reproduces the committed runs exactly). Fed DFN's own cycle-99 lithium loss, the map's fade from cycle 10 to 100 is within a mean 0.021 of DFN on Ai2020@0.3x, 0.045 on Chen2020@0.5x, 0.051 on NCA_Kim2011@1x and 0.120 on OKane2022@1x (under-predicting there, as 5r saw over 20 cycles). Fed the power law it is off by 0.43, 0.34, 0.37 and 0.08. The power law over-predicts the cycle-99 loss by a median 1.93, 1.91, 1.36 and 1.61 times because plating slows down: the local exponent falls from 0.77 to 0.95 over cycles 2 to 10 to 0.24 to 0.63 over cycles 50 to 99 on the graphite cells (0.24 to 0.37 falling to 0.14 to 0.16 on NCA_Kim2011).
  • Reading: 5r's decomposition holds at 100 cycles where the cell runs near open circuit (mean error 0.02 to 0.05 on three of four conditions), so the remaining problem is the lithium-loss rate, which decelerates in a way ten cycles do not show. A predictor needs a self-limiting loss law (plating that slows as the negative empties, which 5q's OCP-rise term tried on SPMe's plating) fitted to the early curve, or a later rung (cycle 20 or 30) where the deceleration has begun. Until then 5o's salt floor plus 5n's union screen stays the procedure.
  • Caveats: committed pools (truth read by 5b to 5o; the predictor's output was not); the diagnostic is 27 designs on four conditions, chosen after the verdicts; plating parameters are OKane2022's on six of seven sets; one PyBaMM version (26.10.1.1).
  • Output: experiments/mapscreen/bench.jsonl, balance.jsonl, ocp.json, diag.jsonl, results.txt, summary.json, mapscreen.svg.

2026-11-15 · Milestone 5s: does 5r's balance map, fed a power law of ten DFN cycles' own lithium loss, predict 100-cycle DFN energy well enough to be the union screen's fade list? (plan, written before any ten-cycle run's lithium curve was read; H108 to H111 are this entry's)

  • Question: 5r split fade into a design-only electrode-balance map and a lithium-loss rate, but fed the map DFN's own 20-cycle loss. 5n's union screen already runs every design to cycle 10, so its lithium curve is free. If a power law through that curve, mapped to energy with 5r's map, predicts cycle 100, it can replace 5n's sqrt(cycle) energy extrapolation as the fade list at almost no cost (the map, about 0.05 s per design).
  • Predictor, fixed now (experiments/mapscreen/run.py): L(n) = a n<sup>b</sup>, log-log least squares through the run's "Total lithium lost [mol]" at the end of cycles 2 to 10 (parallel count included, 5p); predicted cycle-100 Wh/kg = cycle-10 Wh/kg × E_ocv(n_Li − L(99)) / E_ocv(n_Li − lost by end of cycle 9), with E_ocv 5r's open-circuit energy between the cut-offs (cycle n's discharge holds the lithium left after cycle n−1). No fitted constant, no rate term. A run with fewer than three positive loss points is predicted not to fade.
  • Conditions, fixed now by a rule on committed data: every committed 100-cycle pool whose median DFN fade from cycle 10 to 100 is at least 0.2 and whose DFN-best design ranks below 4th by raw cycle-10 Wh/kg (so the union's fade list has to carry it): 17 conditions, 1,108 designs (Ai2020 0.25× to 0.625×, eight; Chen2020 0.5×, 1×, 2×; NCA_Kim2011 0.5×, 0.75×, 1×; OKane2022 1×, 1.25×, 2×). The 100-cycle truth was read by milestones 5b to 5o; the lithium curves and the predictor's output on them were not.
  • Runs: DFN with SEI + plating (5r's both, TR.OPTS) to cycle 10 on every design, one fresh process per run, 4 workers; check: cycle-10 Wh reproduces the committed run's (a smoke run on Chen2020@1x design 0 matched exactly).
  • Comparator: 5n's sqrt fit (a line in √n through cycles 5 to 10 of the energy, read at 100) and 5n's union (top 4 raw plus top 4 sqrt).
  • H108 (ranks): Spearman(map prediction, DFN@100) above the sqrt fit's on at least 12 of 17 conditions. Refuted if on 8 or fewer.
  • H109 (fade size): median over designs of |predicted − DFN fade from cycle 10 to 100| below the sqrt fit's on at least 12 of 17. Refuted if on 8 or fewer.
  • H110 (screen): the union of the top 4 raw and the top 4 by the map is within 1% of the pool's DFN best on every condition. Refuted if above 3% on any.
  • H111 (against 5n): that union's gap is no larger than 5n's union's on every condition. Refuted if larger by more than 1 point on any.
  • Caveats fixed now: committed pools only (seen truth, unseen predictor); the map is open-circuit, so 5r's H107 says it should over-predict fade on designs far from open circuit (NCA_Kim2011); plating parameters are OKane2022's on six of seven sets; one PyBaMM version (26.10.1.1).
  • Script: experiments/mapscreen/run.py; outcome logged above this entry.

2026-11-14 · Milestone 5r outcome: an electrode-balance map with no fitted constant turns each DFN run's own lithium loss into its energy fade within 0.05 on 34 of 40 fresh fading designs, ranks fade within a condition at least as well as the lithium share on all 5 fading conditions (Ai2020@0.3x +0.95 against +0.48), and errs where the design runs far from open circuit (Spearman −0.73). H104 to H107 supported

  • Bench: 128 DFN runs (8 conditions x designs 5 to 12 by j x {SEI + plating, neither}), 20 cycles, 670 s of solver time, about 13 minutes wall on 4 cores (3 workers). None failed; three no-degradation runs stopped early (Ecker2015@1x designs 5 and 6 at cycles 16 and 18, Mohtat2020@1x design 11 at cycle 8), so 61 designs were scored, 40 fading (lithium loss from cycle 2 to 20 above 3% of n_Li; all on Ai2020, Chen2020, NCA_Kim2011 and OKane2022). The map costs about 0.05 s per design after a one-off 4 s per set for the OCP tables.
  • H104 supported: |map − DFN added fade| ≤ 0.05 on 34 of 40 fading designs (0.85; bar 0.75). The six misses: four NCA_Kim2011@1x designs (over-predicted by 0.08 to 0.24) and two on Ai2020@1x (designs 8 and 10, over by 0.065 and 0.063). All six have E2 / E_ocv between 0.16 and 0.56; five are below 0.32.
  • H105 supported: mean absolute error 0.038 against the proportional baseline's 0.053 (ratio 0.71; bar 0.75); medians 0.029 against 0.032. By condition the map wins clearly on Ai2020 (0.3x: 0.012 against 0.049; 1x: 0.033 against 0.086), ties on Chen2020@1x (0.030 against 0.033) and NCA_Kim2011@1x (0.083 against 0.082), and loses on OKane2022@1x (0.032 against 0.017), where it under-predicts every design by a median 0.035; it under-predicts Chen2020@1x by a median 0.029.
  • H106 supported: Spearman(map, DFN added fade) ≥ Spearman(LLI share, DFN added fade) on 5 of 5 fading conditions: Ai2020@0.3x +0.95 against +0.48, Ai2020@1x +0.81 against +0.21, NCA_Kim2011@1x +0.79 against +0.69, OKane2022@1x +0.38 against +0.36, Chen2020@1x +0.10 against +0.10 (a tie, which the plan counts).
  • H107 supported: Spearman(E2 / E_ocv, |map error|) = −0.73 over the 40 (bar ≤ −0.3). The worst misses are the designs DFN delivers least of their open-circuit energy: NCA_Kim2011@1x designs 7, 9 and 11 at E2 / E_ocv 0.19, 0.25 and 0.16, over-predicted by 0.24, 0.08 and 0.20. Such a design is rate-limited (salt or solid diffusion) at this current, so lithium it loses comes out of capacity it was not reaching anyway.
  • Reading: the fade decomposes. On designs that run near open circuit (E2 / E_ocv above about 0.6), lost energy is a design-only function of lost lithium, and that function is the electrode balance: how far the negative's excess and the cut-offs let the window slide before it shrinks. That is why energy fade per unit of lithium varies twofold within a pool (5q) and why the lithium-loss rate alone does not rank it. On Ai2020, the fade-limited cell where 5o's front and 5q's predictor failed, the map ranks fade at +0.81 to +0.95. What it does not give: the lithium-loss rate (still simulated here, from DFN itself), and a rate term for designs far from open circuit, where a constant does as well or better. The consistent under-prediction on OKane2022 and Chen2020 (both graphite-SiO<sub>x</sub> against NMC811 in PyBaMM, CC-only protocol at E2 / E_ocv about 0.5 to 0.6) is the same rate effect in the other direction and is not explained here.
  • Caveats: 20 cycles, not 100; the map is fed DFN's own lithium loss, so this is a decomposition test, not a predictor; plating parameters are OKane2022's on six of seven sets (5p); one PyBaMM version (26.10.1.1); open-circuit window only. The 40 fading designs come from 5 conditions, 8 each, so per-condition Spearman values carry wide intervals.
  • Output: experiments/balance/bench.jsonl, balance.jsonl, ocp.json, results.txt, summary.json, balance.svg.

2026-11-14 · Milestone 5r: does an electrode-balance map turn the lithium a DFN design loses into the energy it loses? (plan, written before the fresh bench's results were read; H104 to H107 are this entry's)

  • Question: 5q found that energy lost per unit of lithium lost varies about threefold within one pool, so the lithium-loss rate alone cannot rank fade, and asked for an electrode-balance map. If such a map, with no simulation, turns each DFN run's own lithium loss into its energy fade, then the fade problem splits cleanly into a design-only map and a lithium-loss rate, and only the rate needs simulation.
  • The map, fixed now (experiments/balance/run.py): per design, from the parameter set and the design mapping only, the negative and positive lithium capacities Q_n and Q_p (c_max × active fraction × thickness × area × parallel count, mol), the cyclable lithium n_Li (both particles' initial concentrations, which PyBaMM's initial_soc keeps) and the set's two OCP curves (401-point tables). The open-circuit window is where U_p(y) − U_n(x) crosses the lower and upper cut-offs with Q_n x + Q_p y = n_Li; its energy is F Q_n ∫ (U_p − U_n) dx. Predicted fade from cycle 2 to 20 = 1 − E(n_Li − L<sub>18</sub>) / E(n_Li − L<sub>0</sub>), with L<sub>k</sub> the lithium the DFN run (SEI + plating) had lost by the end of cycle k+1 (cycle k's discharge follows cycle k−1's charge). No fitted constant. Baseline: proportional, k × LLI share with k = 1.64, the median over the dev bench's fading designs, fixed now. Target: DFN's degradation-added fade, fade(SEI + plating) − fade(no degradation), as in 5p, so protocol drift is not charged to the map.
  • Seen before this entry (development): 5p's committed bench (8 conditions × designs 1 to 4 by j, 31 scored, 20 fading, i.e. losing more than 3% of n_Li from cycle 2 to 20). There the map is within 0.05 of DFN's added fade on 17 of 20 fading designs (0.85), MAE 0.034 against the baseline's 0.059 (median 0.025 against 0.022), ranks fade within a condition at least as well as the lithium share on 5 of 5 fading conditions (Ai2020@1x +1.00 against −0.60), and errs most where DFN's cycle-2 energy is furthest below the open-circuit energy (Spearman −0.40; NCA_Kim2011@1x, MAE 0.09, E2/E_ocv down to 0.27). A variant whose window shrinks by an overpotential fitted to DFN's cycle-2 energy was worse on dev and is not tested.
  • Fresh bench, fixed now: the same 8 conditions, the next 8 designs by j of each committed pool (positions 5 to 12), DFN for 20 cycles with SEI + plating and with neither (128 runs), 5p's mapping, current and protocol, one fresh process per run. Each run also stores per-cycle Ah and lithium in particles.
  • H104 (the map is right): |map − DFN added fade| ≤ 0.05 on at least 75% of fresh fading designs. Refuted if under 50%.
  • H105 (the balance matters): the map's mean absolute error is below 0.75 of the proportional baseline's on the fresh fading designs. Refuted if not below the baseline's.
  • H106 (it ranks): within each fresh fading condition (at least 3 fading designs), Spearman(map, DFN added fade) ≥ Spearman(LLI share, DFN added fade). Supported if on every such condition; refuted if on half or fewer.
  • H107 (where it fails): across fresh fading designs, Spearman(E2 / E_ocv, |map error|) ≤ −0.3, i.e. the map errs where the design runs far from open circuit. Refuted if ≥ 0.
  • Caveats fixed now: 20 cycles, not 100; the map uses DFN's own lithium loss (it is a decomposition test, not yet a predictor); PyBaMM's plating parameters are OKane2022's on six of seven sets (5p); one PyBaMM version (26.10.1.1); open circuit, so no rate term.
  • Script: experiments/balance/run.py; outcome logged above this entry.

2026-11-14 · Milestone 5q outcome: two SPMe cycles that see lithium plating do not rank the 100-cycle DFN designs; the cycle-2 plating rate does not rank the fade (median Spearman 0.03 on the 24 unseen conditions), a self-limited plating correction makes the ranking worse than SPMe's plain cycle-2 energy on 20 of 24, and SPMe cannot run 456 of the 2,324 designs, the DFN best among them on 7 of 36 pools. H100 to H103 refuted

  • Bench: 2,324 two-cycle SPMe runs with SEI and plating (every committed design of the 36 conditions 5b to 5o ran to 100 DFN cycles), 4 workers, about 35 minutes on 4 cores; 1,868 finished both cycles, 456 failed (SPMe's salt goes negative on high-current pools, as 5d found: 56 of 64 on NCA_Kim2011@1.25x, 42 on Chen2020@2x, 41 on OKane2022@2x). A predictor run cost a median 0.03 to 0.15 of a 100-cycle DFN run's time over a pool (median 0.06 on the unseen 24).
  • H100 refuted: Spearman(p2, DFN fade from cycle 2 to 100) was below 0.3 on 19 of the 24 unseen conditions and at least 0.5 on none (median 0.03, range −0.52 to +0.47). On the 12 seen ones it was 0.31 to 0.84.
  • H101 refuted: the self-limited prediction ranked designs worse than SPMe's plain cycle-2 energy w2 on 20 of 24 unseen conditions (median Spearman 0.58 against 0.82). Carrying cycle 2's loss on unlimited (linear) predicts total loss on most designs (median Spearman −0.08).
  • H102 refuted: keeping the top half by the self-limited prediction (designs it could not run kept too) before the union screen missed the pool's DFN best by more than 1% on 5 of 24 and more than 3% on 2 (Chen2020@1.75x 6.1%, Chen2020@1x 3.6%). The plain union screen's worst is 0.23%.
  • H103 refuted: that cut cost 0.92 to 1.45 of the union screen's wall time (median 1.15), above 0.8 on all 24: the predictor's own cost, charged on every design, is more than the half of the ten-cycle DFN runs it saves, and the designs it cannot run still go to the union.
  • Amended after the verdicts, before this entry: the first report scored gaps against the best of the designs SPMe could run, which hid the 7 pools where SPMe fails on the DFN-best design. Gaps are now against the whole pool's DFN best, with designs whose predictor failed kept by the share cut and left out of top-K lists. No verdict changed (all four were refuted under both).
  • Why it fails (5p's committed plating-only runs, post hoc): energy fade per unit of lithium lost over cycles 2 to 20 ranges from −0.68 to 2.35 across the 20 designs that lost more than 3% of their lithium, and from 0.94 to 2.08 within one pool (Ai2020@0.3x). How much energy a design loses for its lost lithium depends on its electrode balance (which electrode limits capacity, and how much excess lithium the negative holds), so a lithium-loss rate alone cannot rank fade. The per-cycle plating loss also halves over 20 DFN cycles (5p), which the OCP-rise correction captures only weakly on graphite's flat plateau: it predicts a median fade of 0.79 to 0.82 on Ai2020 0.25x to 0.375x against 0.52 to 0.61 measured.
  • Reading: the cheap fade predictor 5p asked for needs an electrode-balance map from lost lithium to lost capacity (PyBaMM's electrode-SOH solver is the natural tool; a scratch try on one Ai2020 design returned non-monotone capacities, so it needs care), not a better plating rate. Until then, 5o's salt floor plus 5n's union screen stays the procedure: it is exact or within 0.32% on all 36 conditions, and nothing here is cheaper.
  • Caveats: committed pools only; the 24 unseen conditions are mostly energy-decided, so H102 tested the cut's safety more than the fade regime; SPMe's plating, not DFN's; one PyBaMM version (26.10.1.1); 20% of designs have no SPMe prediction at all.
  • Output: experiments/plating/predict.jsonl, dev.txt, dev.json, plating.svg.

2026-11-14 · Milestone 5q: can two SPMe cycles that see lithium plating predict the 100-cycle DFN fade, and cut the pool before any DFN run? (plan, written before the predictor's results on 24 of the 36 conditions were read; H100 to H103 are this entry's)

  • Question: 5p showed every fade number in the programme is lithium plating, and 5o's zero-simulation (U, r_kt) front misses by up to 4.7% where fade decides (low-current Ai2020, best design on layers 4 to 7), because it ranks high energy first. 5p's next step asked for a near-zero-simulation plating predictor tested as a pool cut.
  • The predictor, fixed now (experiments/plating/run.py): SPMe with the programme's options (solvent-diffusion SEI and irreversible plating, TR.OPTS), 5m's current mapping and CC protocol, two cycles. From it: w2, SPMe's cycle-2 Wh per kg of stack; r2, lithium lost during cycle 2 (mol; "Total lithium lost [mol]", which carries the parallel count, 5p); p2 = r2 over the initial inventory. Three predicted cycle-100 Wh/kg, none with a fitted constant: w2; linear, w2 × (1 − 98 r2 F / Ah2); and limited, the same with the loss integrated under PyBaMM's own irreversible plating law, j ∝ exp(−α F Δφ / RT), with Δφ raised by the negative OCP's rise as lost lithium leaves it emptier at the end of each charge (U(θ<sub>end</sub> − L / Q<sub>n</sub>) − U(θ<sub>end</sub>), from the run's end-of-charge stoichiometry and the set's OCP function).
  • Seen before this entry (development, scratch): on the 11 Ai2020 pools and Chen2020@0.5x, Spearman(p2, DFN fade from cycle 2 to 100) was +0.31 to +0.65; on Ai2020 0.25x to 0.375x Spearman with DFN@100 was w2 −0.06 to +0.51, limited +0.13 to +0.35, and limited over-predicts the median fade (0.79 to 0.82 against 0.52 to 0.61). On 5p's committed bench, the energy fade per unit of lithium lost varies about threefold between designs of one pool (Ai2020@0.3x), so the lost lithium alone cannot rank them. The predictor's runs on the other 24 conditions (Chen2020 1x to 2x, Ecker2015, Marquis2019, Mohtat2020, NCA_Kim2011, OKane2022) had not been read.
  • Procedures scored (no tuning): DFN@100 on the top K = 3, 4, 6, 8 by each predicted score; keep the top half (or quarter) by each, then 5n's union screen on them. The predictor's measured time is charged on every design.
  • H100 (the cycle-2 rate ranks the fade): Spearman(p2, DFN fade 2 to 100) ≥ 0.5 on every unseen condition. Refuted if below 0.3 on any.
  • H101 (plating improves the ranking): Spearman(limited, DFN@100) ≥ Spearman(w2, DFN@100) on every unseen condition. Refuted if lower on more than half.
  • H102 (a cut that keeps the best): keep the top half by limited, then the union screen: gap ≤ 1% on every unseen condition. Refuted if above 3% on any.
  • H103 (and pays): its wall time ≤ 0.6 of the plain union screen's on every unseen condition. Refuted if above 0.8 on any.
  • Also reported, no verdicts: all 36 conditions; the seen 12 separately; 5p's energy fade per lithium lost, design by design.
  • Caveats fixed now: committed pools only, no fresh bench; the 24 unseen conditions are mostly ones where energy already decides (the best sits on (U, r_kt) layer 1 to 3), the exceptions Mohtat2020@3x (layer 7) and NCA_Kim2011@0.5x, so H102 and H103 test safety more than the fade-limited regime; one PyBaMM version (26.10.1.1); SPMe's plating, not DFN's.
  • Script: experiments/plating/run.py; outcome logged above this entry.

2026-11-14 · Milestone 5p outcome: lithium plating makes the DFN designs fade, not SEI. Plating alone reproduces 0.998 to 1.015 of the degradation-added fade on the five conditions that fade, SEI alone 0.000 to 0.006; and PyBaMM's side-reaction lithium variables under-count by exactly the parallel-electrode count (34 on Ai2020)

  • Bench: 128 DFN runs (8 committed conditions x the first 4 designs of each pool x {SEI + plating, plating, SEI, neither}), 20 cycles, 504 s of solver time, about 8 minutes wall on 4 cores (3 workers). One run stopped at cycle 10 (Ecker2015@1x design 2, no degradation), so that design was dropped: 31 designs scored.
  • H96 supported: (Total lithium lost) / (Total lithium lost to side reactions) / (parallel-electrode count) = 1.00000 on all 93 degraded runs (34.0000 raw on every Ai2020 run, 1.0000 elsewhere).
  • H97 supported: on the five conditions where degradation adds more than 1% fade from cycle 2 to 20 (OKane2022@1x 13.4%, Ai2020@0.3x 17.3%, Ai2020@1x 5.2%, Chen2020@1x 12.8%, NCA_Kim2011@1x 24.5%), plating alone reproduces a median 1.002, 0.999, 1.015, 1.000 and 0.998 of it.
  • H98 supported: SEI alone's share is 0.006, 0.002, 0.000, 0.004 and −0.002 on the same five. By cycle 20, SEI took 0.007% to 0.15% of the lithium inventory; plating took 7.8 to 13.2% on the four graphite conditions that fade and 33.7% on NCA_Kim2011@1x.
  • H99 supported: the closed form L<sup>2</sup> = L0<sup>2</sup> + 2 V D c_sol t / z, times z a / V and the electrode volume (parallel count included), matches the SEI-only run's total lithium lost to a relative error under 1e-4 on all 31 runs (rounds to 0.0000).
  • Also seen: Ecker2015, Mohtat2020 and Marquis2019 barely fade at 1x (degradation adds −1.4% to +0.4%, plating 0.5 to 0.7% of inventory), so they were not scored. Without degradation the energy still drifts on Ai2020@1x (+1.6% fade) and NCA_Kim2011@1x (−5.0%, energy rises), the CC-only protocol settling into its cycle; on the rest it is flat after cycle 2.
  • Post hoc (after the verdicts): in the plating-only runs, lithium lost grows as about n<sup>0.83 to 0.90</sup> from cycle 5 to 20 on OKane2022 and Chen2020, n<sup>0.57 to 0.83</sup> on Ai2020@0.3x, near linear on the three that barely fade, and n<sup>0.20 to 0.28</sup> on NCA_Kim2011, where plating saturates early.
  • Reading: every fade number from 5b to 5o is lithium plating, under OKane2022's plating parameters, which 5b's copy rule gives every set but OKane2022. The sqrt(cycle) law that motivated 5n's fade fit is SEI's, and SEI contributes nothing measurable over 20 cycles; the fit worked on low-current Ai2020 because plating there happens to grow close to sqrt(n) (exponent 0.57 to 0.83), and it was anti-correlated on NCA_Kim2011 because plating there saturates (exponent 0.2 to 0.3). No committed score changes: scores are integrated voltage × current, and no milestone read PyBaMM's loss variables (energy-cell-dfn's diagnostics did, on OKane2022, whose parallel count is 1). What changes is the explanation and the next step: a cheap fade predictor has to predict plating (negative-electrode surface overpotential against Li/Li<sup>+</sup> during charge), not SEI; and because plating is a copied parameter set on six of seven cells, the programme's fade results are a statement about OKane2022's plating kinetics on those geometries, which the paper must say.
  • PyBaMM: "Loss of lithium to {domain} lithium plating [mol]" (base_plating.py, Q = c L_k L_y L_z), the SEI counterparts and their sum "Total lithium lost to side reactions [mol]" omit "Number of electrodes connected in parallel to make a cell", which "Total lithium [mol]" includes, although the source comments say the two "should give same value". A ready-to-file report is experiments/attribution/UPSTREAM.md (filing it is an owner step).
  • Caveats: 31 designs, 20 cycles, the first four of each committed pool; one PyBaMM version (26.10.1.1); PyBaMM's submodels, not a measured cell; the 100-cycle shares are not measured here.
  • Output: experiments/attribution/bench.jsonl, results.txt, summary.json, attribution.svg.

2026-11-14 · Milestone 5p: what makes the DFN designs fade? An ablation of PyBaMM's SEI and plating options, and a check of its lithium bookkeeping (plan, written before the bench; H96 to H99 are this entry's)

  • Question: 5n justified its sqrt(cycle) fade fit by SEI growth ("the first fade term in PyBaMM's degradation model"), and 5o's next step asked for a cheaper fade predictor. Every milestone since 5b runs DFN with {"SEI": "solvent-diffusion limited", "lithium plating": "irreversible"}. Which of the two makes the designs fade has never been measured.
  • Seen before this entry (scratch, not committed; PyBaMM 26.10.1.1): (1) PyBaMM's own solvent-diffusion law (sei_growth.py: j_sei = −F c_sol D / L) integrates to L(t)<sup>2</sup> = L0<sup>2</sup> + 2 V D c_sol t / z, independent of potential and current. On the 2,132 development designs its per-condition median is under 0.5% of capacity over 100 cycles on every set but NCA_Kim2011 (1.8 to 3.9%), about 0.2 to 0.5% on Ai2020, against 55 to 65% energy fade at cycle 100 in the Ai2020 benches. (2) On one Ai2020@0.3x design over 3 DFN cycles, "Total lithium lost [mol]" was 34.0 times "Total lithium lost to side reactions [mol]"; with SEI alone the particles lost 0.009% of their lithium, with plating alone 2.6%, with neither 0. (3) On default Ai2020 (34 parallel electrodes) and OKane2022 (1, then set to 5) the ratio equals the parallel-electrode count to four decimals: the "Loss of lithium to ... [mol]" variables multiply by electrode height × width (base_plating.py, Q = c L_k L_y L_z) but not by the parallel count, which "Total lithium [mol]" includes. No milestone score reads those variables (scores are trapezoid Wh from voltage and current), and energy-cell-dfn's diagnostics read them on OKane2022 only (one electrode), so no committed number changes.
  • The procedure, fixed now (experiments/attribution/run.py): 8 committed conditions, one per parameter set at 1x plus Ai2020@0.3x (OKane2022@1x, Ai2020@0.3x, Ai2020@1x, Chen2020@1x, Ecker2015@1x, NCA_Kim2011@1x, Mohtat2020@1x, Marquis2019@1x); the first 4 designs (by j) of each committed pool; DFN for 20 cycles under four option sets (both, SEI only, plating only, none), mapping, current and protocol 5g's, unchanged. Fade is 1 − Wh(cycle 20) / Wh(cycle 2) (cycle 1 starts from the set's own initial state, which a CC-only charge does not return to). Degradation-added fade = fade(both) − fade(none); each option's share = (fade(option) − fade(none)) / added. A design counts only if all four runs finish 20 cycles; condition values are medians over its designs; H97 and H98 score conditions where degradation adds more than 1% fade.
  • H96 (bookkeeping): on every degraded run, (Total lithium lost) / (Total lithium lost to side reactions) / (parallel-electrode count) is within 1e-3 of 1. Refuted if any differs by more than 1e-2.
  • H97 (plating drives the fade): plating alone reproduces at least 0.9 of the degradation-added fade on every scored condition. Refuted if below 0.7 on any.
  • H98 (SEI does not): |SEI alone's share| is below 0.1 on every scored condition. Refuted if above 0.3 on any.
  • H99 (the closed form is PyBaMM's SEI): the closed-form SEI lithium at the SEI-only run's elapsed time is within 10% of that run's total lithium lost, on every run. Refuted if off by more than 25% on any.
  • Caveats fixed now: 32 designs over 8 conditions, 20 cycles (not 100); one PyBaMM version (26.10.1.1); the ablation measures PyBaMM's submodels, not a measured cell; sets that lack plating and SEI parameters carry OKane2022's (5b's copy rule), so "plating drives the fade" is a statement about those copied parameters on every set but OKane2022.
  • Amended after the bench started, before any result was read: the first bench ran the 128 runs in a process pool, and a worker died abruptly after 24 runs (pool broken; those 24 rows were kept). The rest ran as one fresh process per run (as 5b to 5o do), so a crash fails one run, not the bench. No run failed that way.
  • Script: experiments/attribution/run.py; outcome logged above this entry.

2026-11-14 · Milestone 5o outcome: a closed-form salt floor (drop designs with r_kt < −0.2 before any DFN run) kept the DFN-best design on all three fresh pools and cut 5n's union screen to 0.48 to 0.79 of its time (0.15 to 0.20 of all-DFN); the plain (U, r_kt) front cut stays rejected, because where fade decides the best design sits on layers 4 to 7

  • Bench: 192 runs (64 Sobol seed-13 designs x one chunked, resumed DFN run to 100 cycles x NCA_Kim2011@0.875x, Chen2020@1.75x, Ai2020@0.875x), 3 workers, about 20 minutes on 4 cores, none failed or dropped. r_kt cost a median 0.042 to 0.044 s per design, as in development.
  • H92 supported: the floor screen's answer is the pool's DFN@100 best on all three (gap 0, 0, 0; bar 1%).
  • H93 supported: the best design's r_kt is +0.31, −0.04 and +0.36, all above −0.2; the floor dropped 35, 26 and 25 of 64 designs (lowest r_kt −1.54, −1.00, −2.57).
  • H94 supported: wall time 0.57, 0.48 and 0.79 of the plain union screen's (bar 0.80), or 0.152, 0.158 and 0.197 of all-DFN@100 against the union's 0.266, 0.328 and 0.249.
  • H95 supported: the floor screen's gap equals the union's on all three (both exact).
  • Also seen: a floor at 0 would have missed by 9.3% on Chen2020@1.75x, where the best design's r_kt is −0.04, so the floor has to sit below 0 (as development said: the best design sits at or just past the salt edge on high-current pools). The 3-layer front cut was exact on all three here (the best sat on layer 1 or 2), at 0.15 to 0.27; 5m's ladder was exact at 0.22 to 0.26; 5k's front with DFN@100 missed by 1.4% on NCA_Kim2011@0.875x.
  • Over all 36 conditions seen (33 development, 3 fresh): the floor screen is exact on 32, worst 0.32%, the same answers as the union on every one; it costs 0.41 to 1.03 of the union's time (above 1 only where no design is below the floor, by the 0.04 s per design r_kt takes).
  • Reading: a design search does not need a simulation to discard designs that will badly starve their electrolyte. 5i's closed-form salt number is cheap (0.04 s against about 7 to 25 s for a 100-cycle DFN run) and the best design never sat below r_kt −0.08 on 36 pools, while up to 89% of a high-current pool does. The floor's saving is largest exactly where the union screen was dearest on high-current pools (half its time on Chen2020@1.75x) and zero on the low-current Ai2020 pools, where nothing is starved and fade decides; those stay at 0.25 to 0.31 of all-DFN, and need a cheaper fade predictor, not a salt one. The (U, r_kt) front is the wrong zero-simulation cut for that reason: it ranks high energy first, and on fade-limited cells high energy fades fastest.
  • Caveats: three fresh conditions, all at currents where the floor bites and none in the low-current fade regime (so H92 tested the floor's safety, not the union's hard cases); one PyBaMM version (26.10.1.1); one 4-core machine; the floor was picked on development data; r_kt is SPMe's closed-form salt minimum, not DFN's; fade is PyBaMM's SEI and plating submodels.
  • Output: experiments/frontcut/urkt.jsonl, rkt_time.json, dev.txt, dev.json, probe.json, bench.jsonl, results.txt, summary.json, frontcut.svg.

2026-11-14 · Milestone 5o: can the zero-simulation numbers cut the pool before any DFN run? Not the (U, r_kt) front, which drops the best design where fade decides; a salt floor (r_kt ≥ −0.2) before 5n's union screen instead (plan, written before the fresh bench; H92 to H95 are this entry's)

  • Question: 5n's union screen cannot cost less than ten DFN cycles of every design (0.15 to 0.17 of a 100-cycle run each), and its next step asked for a zero-simulation first cut, naming 5k's (U, r_kt) Pareto front. U (thermodynamic Wh/kg over stack mass) and r_kt (5i's closed-form minimum salt ratio) need parameter values only.
  • Seen before this entry (development, experiments/frontcut/dev.txt, all 33 conditions of 5b to 5n; U and r_kt recomputed for all 2,132 designs, urkt.jsonl, and identical to 5l's stored values on its 192): the front cut fails where it would pay. On Ai2020 at 0.25x to 0.75x and Mohtat2020@3x the pool's DFN@100 best sits on (U, r_kt) layer 4 to 7, at U percentile 0.08 to 0.31, because the high-energy designs that dominate it fade fastest. Keeping 3 layers before the union misses by up to 4.7% (exact on 24 of 33), 6 layers by up to 1.3% (28 of 33); a two-corner front (layers of (U, r_kt) and of (−U, r_kt)) is no better (up to 4.7%). What does hold: the best design's r_kt was −0.08 or higher on every one of the 33 conditions (lowest OKane2022@1.75x −0.08, NCA_Kim2011@1.25x −0.06), while up to 89% of a high-current pool sits below −0.1. A salt floor dropping designs with r_kt below −0.5, −0.3, −0.2, −0.15 or −0.1 keeps the union's exact record (29 of 33, worst 0.32%), and a floor at 0 does not (worst 10.7%). At −0.2 it costs 0.41 to 1.03 of the union's wall time (median 0.97; r_kt measured at 0.043 s per design, rkt_time.json, charged on every design): it saves 31 to 59% on the high-current OKane2022, NCA_Kim2011 and Chen2020 pools and costs up to 3% more where nothing is starved. −0.2 was picked as the cheapest floor with a margin of at least 0.1 below the lowest best seen, so it is fitted, and the fresh conditions are its test.
  • The procedure, fixed now (experiments/frontcut/run.py, floor_union, TAU = −0.2): compute r_kt for every design; drop designs with r_kt < −0.2; on the rest run 5n's union screen unchanged (DFN to cycle 10; resume to 100 the top 4 by cycle-10 Wh/kg and the top 4 by the sqrt(cycle) extrapolation of cycles 5 to 10; answer the best DFN@100 among them). Wall time: the measured r_kt time on every design plus the kept designs' measured segments as 5n charges them.
  • Fresh conditions, fixed before any run and chosen only by the floor's predicted share on the new designs (zero simulation): NCA_Kim2011@0.875x (0.55 of designs below the floor), Chen2020@1.75x (0.41) and Ai2020@0.875x (0.39), currents no milestone ran. 64 Sobol designs, scrambled, seed 13 (not used before); one DFN run per design in 10-cycle chunks to 100, each resumed from the last (5m's _child, unchanged), 3 at a time; designs that fail before cycle 100 are dropped as in 5m and 5n. A condition is kept if its DFN probe passes (probe.json).
  • H92 (answer): the floor screen's answer is within 1% of the pool's DFN@100 best on every fresh condition. Refuted if more than 3% below on any.
  • H93 (the floor is safe): the pool's DFN@100 best has r_kt ≥ −0.2 on every fresh condition. Refuted if below on any.
  • H94 (it pays where it bites): its wall time is at most 0.80 of the plain union screen's on every fresh condition. Refuted if above 0.95 on any.
  • H95 (no worse than the union): its gap minus the union's gap is at most 0 on every fresh condition. Refuted if larger by more than 1 point on any.
  • Also reported, no verdicts: the 3-layer front cut, floors from −0.5 to 0, 5m's ladder, 5k's front with DFN@100, the best design's (U, r_kt) layer and U percentile.
  • Caveats fixed now: three conditions, 64 designs each; one PyBaMM version (26.10.1.1); one 4-core machine's timings; the floor was picked on development data; r_kt is SPMe's closed-form salt minimum, not DFN's; fade is PyBaMM's SEI and plating submodels.
  • Script: experiments/frontcut/run.py; outcome logged above this entry.

2026-11-14 · Milestone 5n outcome: ten DFN cycles plus a sqrt(cycle) fade fit find the best design to within 0.16% on three fresh pools, where the raw 10-cycle screen missed by 9.2% and 3.9%; the extrapolation lifts the low-current Ai2020 ranking from Spearman 0.10 and 0.48 to 0.57 and 0.63, but the screen costs 0.24 to 0.32 of all-DFN, not under 0.30

  • Bench: 192 runs (64 Sobol seed-12 designs x one chunked, resumed DFN run to 100 cycles x Ai2020@0.275x, Ai2020@0.35x, NCA_Kim2011@1.25x), 3 workers, about 45 minutes on 4 cores, none killed. On Ai2020@0.275x 13 of 64 designs failed in the first cycle (IDA error-test failures, as at 0.25x and 0.3x) and 5 on Ai2020@0.35x; they were dropped. The probe keep rule was amended before the bench (probe.json, kept_note): SPMe, which this milestone never runs, failed at NCA_Kim2011@1.25x and DFN passed.
  • H87 supported: the union screen's answer is 0.16% short of the pool's DFN best on Ai2020@0.275x and exact on Ai2020@0.35x and NCA_Kim2011@1.25x (bar 1%). 5l's fixed DFN@10 top-3 screen missed by 9.2% and 3.9% on the two Ai2020 pools.
  • H88 supported: Spearman(extrapolated, DFN@100) 0.57 against the raw cycle-10 energy's 0.10 on Ai2020@0.275x, and 0.63 against 0.48 on Ai2020@0.35x. On NCA_Kim2011@1.25x it is -0.68 against 0.97 (the raw list carried that pool, as planned; the sqrt top 3 alone missed by 52%).
  • H89 mixed: wall time 0.315, 0.286 and 0.239 of all-DFN@100 (bar 0.30, refutation 0.40). The first 10 cycles cost a median 0.15 to 0.17 of a 100-cycle run, as 5m measured, so 64 designs to cycle 10 plus 8 to 100 lands near 0.3 on the slow Ai2020 runs.
  • H90 mixed: gap minus 5m's ladder's gap +0.0016 (Ai2020@0.275x, where the ladder was exact), -0.0039 (Ai2020@0.35x, where the ladder missed by 0.39%) and 0. The ladder cost 0.294, 0.265 and 0.207, less than the union on every pool.
  • H91 supported: raw cycle-10 Spearman 0.10 and 0.48 on the two Ai2020 pools, so both sit in the hard regime.
  • Where the best sat: on Ai2020@0.35x it ranked 22nd by raw cycle-10 energy and 3rd by the extrapolation, the case the extrapolation was meant to catch. On Ai2020@0.275x it ranked 8th on both lists, so neither top 4 held it, and the 0.16% miss is the next design. On NCA_Kim2011@1.25x it ranked 1st raw and 58th extrapolated.
  • Over all 33 conditions seen (30 development, 3 fresh): the union is exact on 29, worst 0.32%; the ladder on 30, worst 2.7%; the fixed DFN@10 screen on 24, worst 9.2%.
  • Reading: on these cells a sqrt(cycle) line through cycles 5 to 10 does carry information about late fade that the raw energy lacks, and only where it matters: it helps on low-current Ai2020 and is anti-correlated on NCA_Kim2011, whose fade curves are not sqrt-shaped over 100 cycles. Keeping both lists makes the screen robust on every pool seen so far (worst 0.32%), at about the ladder's price (both 0.2 to 0.3 of all-DFN). The two are cheap in different places: the ladder does more DFN at cycles 20 to 50, the union at cycle 100. Neither gets below about 0.25 on slow Ai2020 runs, because the first ten cycles of every design already cost 0.15 to 0.17. To go lower, a screen has to run fewer than all designs to cycle 10, for example 5k's zero-simulation (U, r_kt) front as the first cut.
  • Caveats: three conditions (51, 59 and 64 designs after drops); one PyBaMM version (26.10.1.1); one 4-core machine's timings; form, window and M were picked on development data; the sqrt law is PyBaMM's SEI submodel's, not a measured cell's.
  • Output: experiments/latefade/probe.json, bench.jsonl, results.txt, summary.json, dev.txt, dev.json, latefade.svg.

2026-11-14 · Milestone 5n: can the first ten DFN cycles predict late fade? A sqrt(cycle) fit over cycles 5 to 10, extrapolated to 100, beside the raw cycle-10 energy (plan, written before the fresh bench; H87 to H91 are this entry's)

  • Question: 5m's ladder was 2.7% short on Ai2020@0.3x because the best design ranked 28th at cycle 10 and 1st only at cycle 50; its next step asked for a predictor of late fade from early quantities. PyBaMM's SEI submodel, the first fade term on these cells, grows the SEI roughly as the square root of time, so the cheapest predictor is the shape of the first ten cycles: a least-squares line in sqrt(n) through cycles 5 to 10 (after the first-cycle transient), read at n = 100. 5l tried a sqrt line through cycles 2 to 10 alone and found it ranked worse than the raw energy on its fresh pools; this milestone tests it as a second list beside the raw one, not as a replacement.
  • Seen before this entry (development, experiments/latefade/dev.txt, all 30 conditions of 5b to 5m; 5b to 5l charged k/100 of each DFN@100 run, 5m's three at measured segments): the sqrt extrapolation ranks the 100-cycle score better than the raw cycle-10 energy on all four low-current Ai2020 pools (0.25x 0.65 against 0.08, 0.3x 0.76 against 0.24, 0.375x and 0.4375x likewise), but much worse on NCA_Kim2011 (as low as -0.60 at 1x) and Chen2020, so alone it is exact on 17 of 30 (worst 25.9%). The union of the top 4 by raw cycle-10 Wh/kg and the top 4 by the extrapolation, resumed to cycle 100 (4 to 8 designs), is exact on 27 of 30, worst 0.32% (Ai2020@0.3x, where 5m's ladder missed by 2.7%), then 0.23% (NCA_Kim2011@1x) and 0.03% (Ai2020@0.375x), at a median 0.198 of all-DFN@100's wall time (max 0.301, Ai2020@0.3x measured). 5m's ladder on the same 30: 28 exact, worst 2.7%, median 0.195. About two dozen variants were tried on this data (scratch, not committed): K 10 and 20, fit windows from cycle 2 or K/2, sqrt, log, power-law and linear forms, m 2 to 4; the power-law and linear forms rank worse than raw everywhere, and the chosen one is the cheapest with a worst gap under 1%. So its development record is fitted, and the fresh conditions are its test.
  • The procedure, fixed now (experiments/latefade/run.py, union_screen, K = 10, LO = 5, M = 4): DFN to cycle 10 on every design; fit each design's Wh/kg over cycles 5 to 10 with a line in sqrt(n) and read it at 100; resume to cycle 100 the top 4 by cycle-10 Wh/kg and the top 4 by that extrapolation; answer the best DFN@100 among them. Wall time: every design's measured first segment plus the resumed designs' remaining segments.
  • Fresh conditions, fixed before any run: Ai2020@0.275x and Ai2020@0.35x (currents no milestone ran, inside the regime where every rank cut at cycle 10 missed), and NCA_Kim2011@1.25x (a current no milestone ran, on the cell where the extrapolation alone ranks worst, so the union's raw list is what has to carry it). 64 Sobol designs, scrambled, seed 12 (not used before); one DFN run per design solved in 10-cycle chunks to cycle 100, each resumed from the last (5m's _child, unchanged; 5m showed resuming is bit-exact), one fresh process per design, 3 at a time. A condition is kept if its baseline probe passes (probe.json). Amended after the probe and before any bench run: the probe also solved SPMe, which this milestone never uses, and SPMe failed at NCA_Kim2011@1.25x (infeasible at initial conditions) while DFN passed; since only DFN is run here, a condition is kept when its DFN probe passes, so all three stay.
  • H87 (answer): the union screen's answer is within 1% of the pool's DFN@100 best on every fresh condition. Refuted if more than 3% below on any.
  • H88 (the predictor sees late fade): Spearman(sqrt-extrapolated cycle-100 Wh/kg, DFN@100) exceeds Spearman(cycle-10 Wh/kg, DFN@100) on both fresh Ai2020 conditions. Refuted if it is no higher on either; mixed otherwise.
  • H89 (price): its wall time is at most 0.30 of all-DFN@100's on every fresh condition. Refuted if above 0.40 on any.
  • H90 (against 5m's ladder): its gap is no larger than the ladder's on every fresh condition. Refuted if larger by more than 1 point on any.
  • H91 (the fresh Ai2020 currents are in the hard regime, so the test means something): Spearman(cycle-10 Wh/kg, DFN@100) is below 0.85 on at least one fresh Ai2020 condition. Refuted if at least 0.92 on both; mixed otherwise.
  • Also reported, no verdicts: the log-form union, the sqrt top 3 alone, 5l's fixed DFN@10 top 3, cycle-20 Spearman, median segment times.
  • Caveats fixed now: three conditions, 64 designs each; one PyBaMM version (26.10.1.1); one 4-core machine's timings; the form, window and M were picked on development data that includes the conditions they were picked to fix; PyBaMM's SEI and plating submodels set every fade number, so the sqrt law is the model's, not a measured cell's.
  • Script: experiments/latefade/run.py; outcome logged above this entry.

2026-11-14 · Milestone 5m outcome: a successive-halving ladder over resumed DFN runs fixes most of the low-current misses (exact on 2 of 3 fresh pools, 2.7% short on Ai2020@0.3x against the 10-cycle screen's 8.8%) but costs 0.24 to 0.29 of all-DFN, not under 0.25; at Ai2020@0.3x the best design ranks 28th of 53 at cycle 10 and 1st only at cycle 50

  • Bench: 216 runs (64 Sobol seed-11 designs x one chunked, resumed DFN run to 100 cycles, plus 8 uninterrupted DFN@100 runs per condition, x Ai2020@0.3x, Ai2020@0.4375x, Ecker2015@0.75x), 3 workers; 3 uninterrupted runs killed for memory and re-run one at a time. On Ai2020@0.3x 11 of 64 designs failed in the first cycle (IDA error-test failures, as 13 did at 0.25x in 5h) and were dropped; none elsewhere.
  • H82 mixed: the ladder's answer is the pool's DFN best on Ai2020@0.4375x and Ecker2015@0.75x and 2.71% short on Ai2020@0.3x (bar 1%, refutation 3%).
  • H83 mixed: wall time over all-DFN@100 0.286, 0.254 and 0.244 (bar 0.25, refutation 0.35). Development's k/100 charge was too low: the first 10 cycles take 0.15 to 0.17 of a 100-cycle run (setup and the first cycle), not 0.10; the same under-charge 5l found for separate DFN@10 runs.
  • H84 supported: gap minus the fixed DFN@10 top-3 screen's gap -0.061, -0.013 and 0 (the fixed screen missed by 8.8% and 1.3% on the two Ai2020 pools).
  • H85 supported: Spearman(cycle-10 Wh/kg, DFN@100) 0.24 on Ai2020@0.3x and 0.76 on Ai2020@0.4375x; so both fresh Ai2020 pools sit in the hard regime. At cycle 20 they are 0.48 and 0.89, at cycle 50 0.91 and 0.98.
  • H86 supported: resumed and uninterrupted runs agree to a relative 0 (bit-identical per-cycle energies) on 7, 8 and 8 checked designs; the resumed run is also cheaper (median 0.97, 0.85 and 0.92 of the uninterrupted run's time), so chunking costs nothing.
  • Post hoc (posthoc.txt, after the verdicts): on Ai2020@0.3x the best design (3) ranks 28th at cycle 10, 23rd at 20 and 1st at 50. No ladder that cuts below about 28 designs at cycle 10 keeps it: keeping 24 at cycle 10, 12 at cycle 20 or 5 at cycle 50 each still miss by 2.7%; keeping 32 then 16 then 4 misses by 0.9% at 0.38 of all-DFN; DFN@50 on all, top 3 to 100, is exact at 0.64. Also: the 5l top-3 stability signal (cycle 5 against 10) said "changing" on all three pools here, including Ecker2015 where every screen was exact, so it does not separate the regimes in either direction.
  • Reading: below about 0.4x on Ai2020 the order of the 100-cycle score is not set until somewhere between cycles 20 and 50, because the designs that start best fade fastest (the green curves cross the orange one after cycle 20 in halving.svg). A rank-based early cut cannot see that crossing; it has to keep the designs long enough to watch it, which on this cell means half the run. Elsewhere (27 of 30 conditions seen so far) the ladder is exact or within 0.25% at about a quarter of all-DFN's time, and resuming makes every rung free of restart cost. What is missing is a predictor of late fade from early quantities (fade rate at cycles 10 to 20, SEI thickness, lithium inventory), tested where fade-curve crossings happen.
  • Caveats: three conditions, 64 designs each (53 on Ai2020@0.3x); one PyBaMM version (26.10.1.1); one 4-core machine; the ladder was picked on development data; degradation is PyBaMM's SEI and plating submodels, not measured fade.
  • Output: experiments/halving/probe.json, bench.jsonl, results.txt, summary.json, dev.txt, dev.json, posthoc.txt, halving.svg.

2026-11-14 · Milestone 5m: where fade keeps growing after cycle 10, does a successive-halving ladder over resumed DFN runs fix 5l's misses? (plan, written before the fresh bench; H82 to H86 are this entry's)

  • Question: 5l's screen (DFN@10 on every design, DFN@100 on the top 3) was exact on its three fresh pools, but in development it missed by 7.2% and 6.0% on Ai2020 at 0.25x and 0.375x, where the cycle-10 ranking falls to Spearman 0.08 and 0.58 against the 100-cycle score. Its next step asked for an adaptive K and for the price of resuming a run instead of restarting it.
  • Resuming, checked before this plan (one design, Ai2020@0.3x, baseline): solving 10 cycles, then 10 more with Simulation.solve(starting_solution=...), gives the uninterrupted 20-cycle run's per-cycle energies to a relative 0 (same model object) or 6e-6 (a new Simulation), and the two segments' times add to the uninterrupted run's (4.5 s + 3.9 s against 8.4 s). So a short run that a screen keeps can be continued, not restarted.
  • Seen before this entry (development, experiments/halving/dev.txt, all 27 conditions of 5b to 5l, resumed runs charged k/100 of each DFN@100 run's time): a stopping signal does not work. On Ai2020@0.25x the top-3 set at cycle 10 equals the one at cycle 5 and Spearman(cycle 5, cycle 10) is 0.94, yet cycle 10 ranks the 100-cycle score at 0.08; an "extend while the top 3 changes" rule (10, 20, 50) kept the 7.2% miss. A schedule with no signal does: DFN to cycle 10 on all, the top 16 resumed to 20, the top 8 to 50, the top 3 to 100 is exact on 26 of 27 (worst 0.23%, NCA_Kim2011@1x) at a median 0.194 of all-DFN@100's time (max 0.216). The fixed screens, also resumed: DFN@10 top 3 exact on 22 (worst 7.2%, 0.15 of the time), DFN@20 top 3 on 24 (worst 2.3%, Ecker2015@0.5x, 0.24), 10->16, 20->3 on 24 (worst 2.3%, 0.17). About a dozen ladders were tried on this data (scratch, not committed: keep counts 8 to 20, rungs 20 to 50); the chosen one is the cheapest seen that is exact on Ai2020@0.25x, 0.375x and Ecker2015@0.5x, so its development record is fitted, and the fresh conditions are its test.
  • The procedure, fixed now (experiments/halving/run.py, halving, PLAN (10, 16), (20, 8), (50, 3)): DFN to cycle 10 on every design; keep the top 16 by cycle-10 Wh/kg and resume them to 20; keep the top 8 and resume them to 50; keep the top 3 and resume them to 100; answer the best DFN@100 among those 3. Wall time: each design's measured segments up to the rung it reached (setup included in the first). Compared with 5l's fixed screen (charged both resumed and as 5l charged it) and all-DFN@100.
  • Fresh conditions, fixed before any run: Ai2020@0.3x and Ai2020@0.4375x (currents no milestone ran, inside the low-current regime where 5l's screen missed and between it and 0.5x), and Ecker2015@0.75x (between 0.5x, where every fixed screen missed by 2.3%, and 1x). 64 Sobol designs, scrambled, seed 11 (not used before); one DFN run per design solved in segments to cycles 10, 20, 50 and 100, each resumed from the last, one fresh process per design, 3 at a time (amended before any fresh result was read: the first bench resumed from the whole solution, which doubled memory and had one run killed at 13 of 15 GB, so it was stopped after 2 designs, deleted, and restarted with 10-cycle chunks on one Simulation object, each resumed from the previous chunk's last_state; on the baseline design this reproduces the uninterrupted run's cycle-20 energy exactly); designs 0 to 7 also get an uninterrupted DFN@100 run (resume check). A condition is kept if its baseline probe passes (probe.json). Simulation, parameters and degradation options imported unchanged from 5g.
  • H82 (answer): the ladder's answer is within 1% of the pool's DFN@100 best on every fresh condition. Refuted if more than 3% below on any.
  • H83 (price): its wall time is at most 0.25 of all-DFN@100's on every fresh condition. Refuted if above 0.35 on any.
  • H84 (against 5l's screen): its gap is no larger than the fixed DFN@10 top-3 screen's on every fresh condition. Refuted if larger by more than 1 point on any.
  • H85 (the fresh Ai2020 currents are in the hard regime, so the test means something): Spearman(cycle-10 Wh/kg, DFN@100) is below 0.85 on at least one of the two Ai2020 conditions. Refuted if at least 0.92 on both; mixed otherwise.
  • H86 (resuming is exact): on the 8 checked designs per condition, the resumed run's per-cycle energies match the uninterrupted run's to a relative 1e-4. Refuted if any differs by more than 1e-2.
  • Also reported, no verdicts: Spearman of cycles 5, 10, 20 and 50 with the 100-cycle score, the top-3 stability signal, DFN@20 top 3, the two-rung ladder, median segment times, resumed against uninterrupted wall time.
  • Caveats fixed now: three conditions, 64 designs each; one PyBaMM version (26.10.1.1); one 4-core machine's timings; the ladder was picked on development data that includes the conditions it was picked to fix; PyBaMM's SEI and plating submodels set every fade number.
  • Script: experiments/halving/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5l outcome: retention needs ten cycles of DFN, not a hundred. On three fresh conditions the cycle-10 energy ranks the 100-cycle score at Spearman 0.92 to 0.97, and the screen (DFN@10 on all, DFN@100 on the top 3) found the pool's DFN best exactly on all three at 0.19 of all-DFN's wall time

  • Bench: 384 runs (64 Sobol seed-10 designs x DFN@100 and a separate DFN@10 x Ai2020@0.625x, NCA_Kim2011@0.75x, OKane2022@1.75x), 3 workers, about 28 minutes on 4 cores, none failed or killed, none dropped. A separate DFN@10 run reproduces the first 10 cycles of the DFN@100 run exactly (max relative difference 0 on all 192 pairs), so a search could stop a run at cycle 10 and resume it.
  • H78 supported: Spearman(cycle-10 Wh/kg, DFN@100 Wh/kg) 0.97 (Ai2020@0.625x), 0.95 (NCA_Kim2011@0.75x), 0.92 (OKane2022@1.75x).
  • H79 supported: the screen's answer is the pool's DFN best on all three (gap 0).
  • H80 supported: its measured wall time is 0.198, 0.192 and 0.187 of all-DFN@100's. A separate DFN@10 run costs 0.14 to 0.15 of a DFN@100 run, not 0.10 (solver setup and the first cycle; development's 10/100 charge was too low, and the margin to 0.25 absorbed it).
  • H81 supported: the screen's gap (0, 0, 0) is no larger than 5k's (U, r_kt) front's (0, 1.13% and 0.16%, at 0.16 to 0.27 of all-DFN's time).
  • Also reported: the sqrt-cycle extrapolation of cycles 2 to 10 ranks worse than the raw cycle-10 energy on all three (+0.40, -0.56, +0.55): the first ten cycles fix the order, not the shape of the fade curve. Cycle-10 retention ranks 100-cycle retention at 0.84 to 0.94. Top 1 alone is exact on two of three (0.7% short on NCA_Kim2011@0.75x) at 0.15 to 0.16 of all-DFN; DFN@10 on the first two (U, r_kt) layers only is exact on all three at 0.11 to 0.12.
  • Reading: of the three factors 5k split the score into, two need no simulation and the third, retention, is set mostly in the first ten cycles on these cells, so a 10-cycle DFN run carries nearly the whole 100-cycle ranking. Combined with 5k's front, the cheapest exact procedure seen on the fresh pools is DFN@10 on the first two (U, r_kt) layers and DFN@100 on the top 3 (0.11 to 0.12 of all-DFN). The development exceptions stand: on Ai2020 at 0.25x and 0.375x, where fade keeps growing after cycle 10, the cycle-10 ranking falls to 0.08 and 0.58 and the screen missed by 7.2% and 6.0%; the fresh Ai2020 rate (0.625x) sits above that regime, so the low-current failure was not re-tested here.
  • Caveats: three conditions, 64 designs each; one PyBaMM version (26.10.1.1); one 4-core machine's timings; K = 10 and m = 3 were chosen on development data; PyBaMM's degradation submodels and parameter sets, not measured fade, set every retention number here.
  • Output: experiments/fade/probe.json, bench.jsonl, results.txt, summary.json, dev.txt, dev.json, fade.svg.

2026-11-13 · Milestone 5l: retention, the factor 5k left to DFN, read off a 10-cycle DFN run? (plan, written before the fresh bench; H78 to H81 are this entry's)

  • Question: 5k split the DFN@100 score into U x utilisation x retention and found the first two need no simulation; retention is what made its zero-SPMe (U, r_kt) front miss by up to 4.7% (5.9% in development), and on Ai2020 it is the binding limit. Its next step asked for a retention predictor. A DFN run's Wh/kg at cycle K is U x utilisation x the retention to cycle K, so the cheapest candidate is a short DFN run. The screen tested here, fixed now (experiments/fade/run.py, screen): DFN@10 on every design, DFN@100 on the top 3 by cycle-10 Wh/kg, answer the best DFN@100 among them. Wall time is charged with separate DFN@10 runs (measured, setup included) plus the top 3 designs' own DFN@100 runs; continuing a run from cycle 10 is not assumed.
  • Seen before this entry (development, experiments/fade/dev.txt, all 24 conditions of 5b to 5k, DFN@10 read as the first 10 cycles of each DFN@100 run and charged 10/100 of its time): Spearman(cycle-10 Wh/kg, DFN@100 score) median 0.956, at least 0.85 on 22 of 24; the two exceptions are Ai2020 at its lowest currents (0.25x 0.08, 0.375x 0.58), where fade keeps growing after cycle 10. The screen finds the pool's DFN best exactly on 19 of 24 (5k's front: 9 of 24), median gap 0, worst 7.2% (Ai2020@0.25x; front 5.7%), at 0.13 to 0.16 of all-DFN@100's wall time (front 0.13 to 0.29). It is worse than the front by more than 3% once (Ai2020@0.375x, 6.0% against 2.7%). A least-squares line in sqrt(cycle) through cycles 2 to 10, extrapolated to cycle 100, ranks worse than the raw cycle-10 energy (median 0.84, as low as -0.84 on NCA_Kim2011@1x): the first ten cycles do not fix the shape of the fade curve, but they do fix most of the ordering. Not tried: a closed-form fade proxy from the SEI and cracking parameters.
  • Fresh conditions, fixed before any run: the two cells 5k named, where energy above the flag does not decide, at currents no milestone ran (Ai2020@0.625x, between development's 2.4% miss at 0.5x and exact at 0.75x; NCA_Kim2011@0.75x), and OKane2022@1.75x (its best sat on the flag in 5j). All three passed the baseline probe (experiments/fade/probe.json). Designs: 64 Sobol designs, scrambled, seed 10 (not used before); DFN@100 and a separate DFN@10 on each, one fresh process per run, 3 at a time. Simulation, mapping and pools imported unchanged from 5g and 5k.
  • H78 (the short run orders the long one): Spearman(cycle-10 Wh/kg, DFN@100 Wh/kg) is at least 0.85 on every fresh condition. Refuted if below 0.5 on any.
  • H79 (the screen's answer): the screen's answer is within 3% of the pool's DFN@100 best on every fresh condition. Refuted if more than 7.5% below on any.
  • H80 (its price, measured): the screen's wall time is at most 0.25 of all-DFN@100's on every fresh condition. Refuted if above 0.40 on any.
  • H81 (against 5k's front): the screen's gap is no larger than the (U, r_kt) front's (DFN@100 on layer 1) on every fresh condition. Refuted if larger by more than 3 points on any.
  • Also reported, no verdicts: the sqrt-cycle extrapolation, top 1 and top 5, DFN@10 restricted to the first two and three (U, r_kt) layers, the measured DFN@10 / DFN@100 time ratio, and the check that a separate DFN@10 run reproduces the first 10 cycles of the DFN@100 run.
  • Caveats fixed now: three conditions, 64 designs each; one PyBaMM version (26.10.1.1); one 4-core machine's timings; K = 10 and m = 3 were picked on development data (K = 5 and 20 were looked at: 5 is as cheap but weaker on Ai2020, 20 costs twice as much for 2 more exact conditions), so the fresh test is the check on that choice.
  • Script: experiments/fade/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5k outcome: the energy optimum sits where the cell's first limit binds. Above the salt flag thermodynamic energy orders first-cycle energy (Spearman 0.99 to 1.00), below it r_kt orders utilisation (0.60 to 0.88), and the two pull against each other; on Ai2020 fade is the first limit and the best moves off the edge (r_kt 0.67)

  • Bench: 389 runs (64 Sobol seed-9 designs x SPMe V0 and DFN@100 x Ecker2015@1.5x, Mohtat2020@3x, Ai2020@0.375x, plus 5 V1 re-solves), 3 workers, none killed. All three passed the probe. Two Ai2020 DFN runs did not reach 100 cycles (designs 9 and 47, dropped). U and r_kt for a pool took 20 to 23 s (0.3 s per design, mostly PyBaMM's parameter evaluation).
  • H74 supported: among sound designs (r_kt >= 0.30; 13, 36 and 42 of them) Spearman(U, BOL Wh/kg) is 0.99, 1.00 and 1.00. Median utilisation 0.85 to 0.96.
  • H75 supported, one at the bar: among starved designs (r_kt <= 0.10; 27, 13 and 10) Spearman(r_kt, utilisation) is 0.82, 0.60 (Mohtat2020@3x) and 0.88.
  • H76 supported: Spearman(U, r_kt) over the pool -0.82, -0.81 and -0.36 (Ai2020 again the weakest, as in development).
  • H77 supported: DFN on the first (U, r_kt) Pareto layer, with no SPMe run, comes within 0.9%, 4.7% and 2.7% of the pool's DFN best at 18, 14 and 11 DFN calls. It is exact on none of the three (development: 9 of 21).
  • Where the best sits: Ecker2015@1.5x r_kt +0.22, U percentile 0.53, retention 0.80; Mohtat2020@3x r_kt +0.12, U percentile 0.59; Ai2020@0.375x r_kt +0.67, U percentile 0.27. The Ai2020 best lies outside 5j's H72 range ([-0.15, 0.65]), the first of 24 conditions to do so: among its sound designs Spearman(U, retention) is -0.94 (development -0.94 to -0.38 on Ai2020), so U buys first-cycle energy and loses it to fade, and U ranks the 100-cycle score at -0.03. On the other two cells retention moves with U (+0.79) or barely at all (+0.14), and the best sits just above the flag.
  • Share of log-score variance (covariance with log score over its variance; sums to 1): Ecker2015@1.5x U 0.21, utilisation 0.42, retention 0.37; Mohtat2020@3x 0.60, 0.14, 0.26; Ai2020@0.375x -0.20, 1.15, 0.05. No verdicts.
  • Post hoc (after the verdicts, posthoc.txt): on the same pools 5j's pre-screen and 5h's band procedure are both exact, at 36, 18 and 40 DFN calls (pre-screen) and 25, 15 and 40 (band), plus SPMe on most designs. The front costs 11 to 18 DFN calls and no SPMe, and gives up 0.9% to 4.7%. Top-U above the flag (k = 5) misses by 0.9%, 4.7% and 6.0%.
  • Reading: the answer to 5j's question. The score is U x utilisation x retention. U and r_kt are both set by the same design moves (thicker, denser electrodes store more and starve sooner), so across a pool they are anti-correlated (-0.36 to -0.87 on 24 conditions). Above the flag utilisation is flat (0.85 to 0.98) and U decides; below it utilisation falls with r_kt; the best is the highest-U design before utilisation falls, which is why it sits at r_kt between about 0 and 0.4. Where fade grows with U (Ai2020) retention is the binding limit instead and the best moves to lower U and higher r_kt. Two of the three factors cost 0.3 s per design with no simulation; the third (retention) is what still needs DFN, and it is what made the front miss by up to 4.7%. For an engineer: r_kt is a design constraint (do not push loading past r_kt about 0), U is the objective up to it, and the DFN runs are best spent on fade.
  • Caveats: three conditions, 62 to 64 designs each; one PyBaMM version (26.10.1.1); U is the parameter set's thermodynamic energy, so a cell with large ohmic or solid-diffusion losses above the flag (NCA_Kim2011@0.5x in development, utilisation 0.80, Spearman 0.52) would break H74; retention is measured, not predicted; H77's 6% bar came from development.
  • Output: experiments/edge/choose.json, probe.json, bench.jsonl, results.txt, summary.json, dev.txt, dev.json, posthoc.txt, edge.svg.

2026-11-13 · Milestone 5k: why does the DFN@100 energy optimum sit at the salt edge? The score split into three factors, two of them from the parameter set alone (plan, written before the fresh bench; H74 to H77 are this entry's)

  • Question: 5j found the pool's DFN best has r_kt between -0.06 and +0.58 on all 21 conditions, inside a pool spanning -3.98 to +0.92, and its next step asked why. The score every milestone ranks by (DFN Wh/kg at cycle 100) factors exactly as U x utilisation x retention: U the design's thermodynamic energy over its stack mass (PyBaMM's calculate_theoretical_energy, SOC 1 to 0, as in 5j's bound), utilisation the first cycle's delivered Wh/kg over U, retention cycle 100 over cycle 1. U and r_kt need no simulation. The claim to test: above the salt flag U orders the designs' first-cycle energy; below it r_kt orders their utilisation; U and r_kt pull against each other across a pool (thicker, denser electrodes store more and starve sooner), so the best sits where the first constraint binds. Retention is the third factor and has no closed form here.
  • Seen before this entry (development, experiments/edge/dev.txt, all 21 conditions of 5b to 5j; the factor split had not been computed before): among sound designs (r_kt >= 0.30, conditions with at least 10) Spearman(U, BOL) median 0.99, range 0.52 (NCA_Kim2011@0.5x, utilisation 0.80) to 1.00; among starved designs (r_kt <= 0.10) Spearman(r_kt, utilisation) median 0.90, range 0.64 to 0.95; Spearman(U, r_kt) over each pool -0.87 to -0.36 (Ai2020 -0.36 to -0.48, every other cell below -0.76). Retention is where the cells differ: Spearman(U, retention) among sound designs runs from -0.94 (Ai2020@0.25x) to +0.90 (OKane2022@1x). On Ai2020 a high-U design loses capacity faster, so its DFN best sits at U percentile 0.14 to 0.31 and well above the flag (r_kt 0.23 to 0.47); on the other cells it sits at U percentile 0.70 to 0.95 and r_kt -0.06 to +0.37. A zero-SPMe shortlist (DFN on the first Pareto layer of (U, r_kt), both maximised) finds the pool best exactly on 9 of 21 conditions, median gap 0.6%, worst 5.9%, at 14.8 DFN calls on average; two layers, 13 of 21 at 28.4 calls (5j's pre-screen: exact on all, 28 to 42 DFN calls plus SPMe).
  • Fresh conditions, chosen by r_kt alone before any run (experiments/edge/choose.json; no labels read): candidates in the listed order (5j's list after the two it used, then two Ai2020 rates no milestone ran), the first three of different cells with at least 10 designs predicted in each regime: Ecker2015@1.5x (27 starved, 13 sound), Mohtat2020@3x (13, 36), Ai2020@0.375x (10, 44). Designs: 64 Sobol designs, scrambled, seed 9 (not used before); SPMe@100 V0 and DFN@100 on each, after a baseline probe, as in 5j. Simulation, mapping and pools imported unchanged.
  • H74 (U orders the sound designs' first cycle): Spearman(U, BOL Wh/kg) among designs with r_kt >= 0.30 is at least 0.85 on every fresh condition with at least 10 of them. Refuted if below 0.5 on any.
  • H75 (r_kt orders the starved designs' utilisation): Spearman(r_kt, utilisation) among designs with r_kt <= 0.10 is at least 0.6 on every fresh condition with at least 10 of them. Refuted if below 0.3 on any.
  • H76 (the two pull against each other): Spearman(U, r_kt) over the pool is at most -0.3 on every fresh condition. Refuted if above 0 on any.
  • H77 (a shortlist with no SPMe run): DFN on the first (U, r_kt) Pareto layer finds a design within 6% of the pool's DFN best on every fresh condition. Refuted if more than 10% below on any.
  • Also reported, no verdicts: Spearman(U, retention) among sound designs, the share of log-score variance each factor carries, where the best sits (r_kt, U percentile, utilisation, retention), the two-layer front and top-U-above-the-flag shortlists, the cost of U and r_kt per pool.
  • Caveats fixed now: three conditions, 64 designs each; one PyBaMM version (26.10.1.1); the regime thresholds are 5i's flag and 6a's 0.30, not tuned; U and r_kt ignore degradation, so retention is measured, not predicted; the shortlist's bar comes from development.
  • Script: experiments/edge/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5j outcome: the salt pre-screen does not make the search cheaper (0.90x and 1.12x the band procedure's time), but it makes it exact: on fresh Chen2020@1.5x the band procedure missed the DFN best by 4.5% and the pre-screen did not; the best design sat on the salt flag on 2 of 2 fresh conditions and 6 of 19 committed ones

  • Bench: 256 runs (64 Sobol seed-8 designs x SPMe V0 and DFN@100 x OKane2022@1.25x and Chen2020@1.5x), 3 workers, none killed, none failed DFN, no SPMe early stops (so no V1 re-solves). Both conditions passed the probe. r_kt for each pool took 3.8 s and 2.6 s.
  • H70 supported: the pre-screen's answer is the pool's DFN best on both (gap 0.0000).
  • H71 mixed: pre-screen wall time over the band procedure's 1.12 on OKane2022@1.25x (28 DFN runs against 22; 53 s of SPMe saved, 6 more DFN runs spent) and 0.90 on Chen2020@1.5x (42 against 36; 86 s of SPMe saved). Neither is outside [0.85, 1.15]. With the 19 development conditions (0.91 to 1.08, median 1.01) the pre-screen neither saves nor costs more than about 12%.
  • H72 supported: the DFN best's r_kt is +0.03 (OKane2022@1.25x, pool -0.42 to +0.58) and +0.08 (Chen2020@1.5x, pool -0.65 to +0.51). Both are flagged.
  • H73 supported: the flag agrees with the 100-cycle SPMe suspect label on 64 of 64 designs on both conditions.
  • What the band procedure did on Chen2020@1.5x (not predicted by any hypothesis): it missed the DFN best by 4.54% (121.8 against 127.6 Wh/kg), as did 5g's iterate step; it is the band stop's first miss on 21 conditions. Mechanism: 5e's rule verifies from the lowest SPMe r_min up and stops after three designs in a row that SPMe scored within 25% of DFN; here that run ended at r_min 0.071, inside the flagged block, one design before the best (design 31, r_min 0.078, SPMe 102.8 against DFN 127.6 Wh/kg: 19% low, so not "mis-scored" by milestone 1's label). Every verified design had r_min <= 0.10, so none was "sound" and the band factor q was floored at 1: the stop had nothing to calibrate SPMe's under-scoring against. The pre-screen verifies every flagged design by construction, so it reached design 31; on that condition it was both exact and cheaper (0.90 of the band's time, 0.93 of all-DFN).
  • Discarding flagged designs instead (no DFN for them) would miss the best by 1.9% and 6.5% on the fresh conditions, and by up to 17.0% on the committed ones (OKane2022@2x). Across 21 conditions the best design is flagged on 8.
  • Post hoc, the thermodynamic bound (PyBaMM's calculate_theoretical_energy from SOC 1 to 0 of each design's parameter values, over the stack mass) against DFN@100 on all 1395 pooled designs: never violated, U/DFN from 1.06 to 14.16 (median 2.89). On the committed pools, 0 of 429 flagged designs have a bound below the pool's DFN best, so a branch-and-bound skip of flagged designs would prune none of them even with the best already known. The plan's dev note (five designs, 4.4 to 8.3) stands as a subset of this.
  • Reading: the closed-form flag does not buy wall time inside the search, because the designs it flags are the ones the rule sends to DFN anyway and SPMe is the cheap part of the bill. What it buys is that every flagged design gets a DFN score, and that matters because the best design in a pool sits at the salt edge: its r_kt lies between -0.06 and +0.58 on all 21 conditions, and below the flag on 8. A reduced-model screen that treats salt depletion as a reason to discard (or as a reason to stop early) loses the design it is looking for. For the paper this replaces the run-of-3 stop inside the flagged block with a rule that has no tuning: DFN on every r_kt-flagged design, the 5e rule and band stop above the flag.
  • Caveats: two fresh conditions, both of them graphite cells already seen at other currents; 64 designs each; the band's miss is one event; timings from one 4-core machine at 3 workers, where SPMe is 0.14 to 0.55 of DFN's time per run (a faster DFN would make the pre-screen relatively dearer); the 25% mis-scored label, the run-of-3 and the 0.10 flag are unchanged from earlier milestones, not tuned here.
  • Output: experiments/prescreen/choose.json, probe.json, bench.jsonl, results.txt, summary.json, dev.txt, dev.json, bound.jsonl, prescreen.svg.

2026-11-13 · Milestone 5j: does 5i's closed-form salt flag, used before any simulation, make the design search cheaper? (plan, written before the fresh bench; H70 to H73 are this entry's)

  • Question: milestone 5i turned the trust flag into a formula, r_kt, that costs 0.05 s per design and reproduces SPMe's minimum salt ratio. Its next step asked to put it in front of the search and price it. If a design is already known to starve its electrolyte, its SPMe run is wasted: the rule will verify it with DFN anyway.
  • The pre-screen procedure, fixed now (experiments/prescreen/run.py, prescreen): (1) compute r_kt for every design in the pool; designs with r_kt <= 0.10 go to DFN@100 and get no SPMe run; (2) the rest get SPMe (V0, V1 re-solve of early stops) and 5e's rule (queue and run-of-3 stop) over them alone; (3) 5h's band stop over the whole pool from the union of both verified sets, with the pre-flagged designs carrying no screen score. Wall time: r_kt (measured) + SPMe on the rest + every DFN run. Compared with 5h's band procedure (SPMe on every design) and all-DFN.
  • Seen before this entry (development, experiments/prescreen/dev.txt, the 19 committed conditions; r_kt was written on these designs in 5i, this procedure's cost had not been computed): answer gap 0 on all 19; wall time against the band procedure median 1.01, range 0.91 to 1.08; against all-DFN at most 1.01. The SPMe time saved on flagged designs is spent again: every flagged design is verified, where the band procedure's run-of-3 can stop inside the flagged block, and the rule's run-of-3 then verifies three more designs above the flag. Two variants were tried on the same data and are not tested here: dropping the rule on the unflagged designs (median 0.93 of the band's time, but it misses the DFN best by 4.4% to 7.2% on all four Ai2020 conditions, where SPMe under-scores sound designs and nothing calibrates the band), and a branch-and-bound skip of flagged designs using the cell's thermodynamic energy (PyBaMM's calculate_theoretical_energy over the stack mass) as an upper bound on DFN@100 Wh/kg (on the five OKane2022@2x designs checked the bound holds but sits 4.4 to 8.3 times above the DFN score, so it would prune nothing; the full check is reported with the outcome). Also seen: the pool's DFN best is itself flagged (r_kt <= 0.10) on 6 of 19 conditions, and its r_kt lies between -0.06 and 0.58 on all 19, while pools span -3.98 to 0.92.
  • Fresh conditions, chosen by r_kt alone before any run (choose.json; no labels read): candidates in the plan's order, the first whose predicted flagged share falls in [0.15, 0.45) and the first, of another cell, in [0.45, 0.80): OKane2022@1.25x (0.375) and Chen2020@1.5x (0.609), multiples of 5b's 48.7 A/m2, neither run before. Designs: 64 Sobol designs, scrambled, seed 8 (not used before), SPMe@100 V0 and DFN@100 on each, V1 re-solves of early stops, one fresh process per run, 3 at a time, after a baseline probe as in 5g. Simulation, mapping, labels and procedures imported unchanged.
  • H70 (answer): the pre-screen's answer is within 1% of the pool's DFN@100 best on both conditions. Refuted if more than 2% below on either.
  • H71 (no saving, as development says): the pre-screen's wall time over the band procedure's lies in [0.90, 1.10] on both. Refuted if below 0.85 or above 1.15 on either; mixed otherwise.
  • H72 (the optimum sits at the salt edge): the pool's DFN best has r_kt in [-0.15, 0.65] on both conditions. Refuted if outside [-0.30, 0.80] on either.
  • H73 (the flag on 100-cycle labels): r_kt <= 0.10 agrees with the 100-cycle SPMe suspect label (V0 fails or whole-run r_min <= 0.10) on at least 95% of designs on each condition. Refuted below 90% on either.
  • Also reported, no verdicts: the gap of a screen that discards flagged designs (best DFN among r_kt > 0.10), calls, the SPMe time saved, the iterate step.
  • Caveats fixed now: two conditions, 64 designs each, one PyBaMM version (26.10.1.1); one 4-core machine's timings; the procedure and H71's range come from the 19 development conditions.
  • Script: experiments/prescreen/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5i outcome: SPMe's salt-depletion flag needs no SPMe run. A closed-form steady state with D_e(c) gives SPMe's minimum salt ratio to within 0.0003 on 408 fresh runs and misclassifies none; the constant-D form ranks as well but over-predicts depletion

  • Bench: 816 fresh runs (4 cells x 6 currents x 17 designs x SPMe V0 and DFN, 2 cycles), 3 workers, none killed; 8 Ramadass2004 DFN runs did not finish 2 cycles (dropped from DFN comparisons only). Committed: 1280 designs over the 19 conditions, scored in 60 s of parameter evaluation. Every committed run's current matched the predictor's to 1e-6.
  • H64 supported: Spearman(r_ss, SPMe r_min) 0.99 pooled, at least 0.77 in every condition (19 of 19 at least 0.6).
  • H65 supported: AUC 0.997; the rule r_ss <= 0.10 misclassifies 13.8% (all on the side of calling a design suspect that is not).
  • H66 mixed: the predicted suspect share is within 0.15 on 12 of 19 conditions. It is always too high: at r_ss 0.1 the median SPMe r_min is 0.26, because D_e rises as the salt empties.
  • H67 supported: AUC for milestone 1's mis-scored label 0.951 against 0.957 for SPMe's own simulated r_min.
  • H68 supported: on the fresh sweep AUC 0.998, misclassification 4.4%, Spearman 1.00; the baseline crossing is predicted at 0.23x (Ramadass2004, every multiple suspect), 0.51x (NCA_Kim2011, observed between 0.5x and 1x), 2.69x (Marquis2019, not crossed by 3x) and 5.0x (Mohtat2020, not crossed by 3x). Three of the four brackets are open-ended, so the crossing part is a weak test, as the plan's factor allowed.
  • H69 supported (the post hoc Kirchhoff form r_kt, registered before the fresh labels were read): on the fresh sweep the rule r_kt <= 0.10 misclassifies 0 of 408 designs, and the mean |max(r_kt, 0) - max(SPMe r_min, 0)| is 0.0003 (linear form 0.034). On the committed data, where it was written, it misclassifies 3 of 1280 (all within 0.001 of the threshold), matches every condition's suspect share within 0.02 (19 of 19 within 0.15), has mean difference 0.0031, gives AUC 0.965 for mis-scoring, and with 5g's gate rule (4 of the first 8 designs suspect) makes the same call as the simulated flag on 19 of 19 conditions (post hoc).
  • Where it departs: the 19 committed designs where SPMe's r_min is more than 0.05 above r_kt are all Ai2020@0.25x runs that stopped in the first cycle, before reaching steady state. The formula gives what a finished run would reach.
  • Against DFN's own minimum: Spearman 0.98 (committed) and 0.91 (fresh), mean absolute difference 0.034 and 0.029. The formula is a model of SPMe's electrolyte, which shares its uniform reaction; DFN's reaction moves away from the depleted collector, so DFN's minimum is higher where SPMe empties.
  • Reading: the trust test of milestones 1 to 5h is a function of the parameter set and the design alone: thicknesses, porosities, Bruggeman exponents, D_e(c) and t+. For a pool of designs it costs about 0.05 s per design, against 1 to 30 s for the SPMe run it replaces, and it gives an engineer a closed-form current at which a design empties its electrolyte under SPMe's assumptions. The screen still needs SPMe's score, but the decision of which designs to verify with DFN, and 5g's skip-SPMe gate, can be made before any simulation. It does not say how far SPMe's score is from DFN's; that is still the DFN run's job.
  • Process note: an early report call, made while the fresh bench had a few dozen rows, wrote a partial fresh.jsonl to disk (committed in the second commit); its fresh section was not printed or read before H69 was registered.
  • Caveats: one PyBaMM version (26.10.1.1), whose SPMe uses the same electrolyte equation the formula solves, so the agreement is by construction up to the transient, t+(c) and solver effects; t+ held at c0; four fresh cells, three of them seen before on other designs; isothermal.
  • Output: experiments/sand/committed.jsonl, bench.jsonl, fresh.jsonl, results.txt, summary.json, sand.svg; derivation in THEORY.md part 3.

2026-11-13 · Milestone 5i: can a closed-form salt-depletion number, computed from the parameter set and the design alone, say where SPMe breaks before any simulation? (plan, written before the run; H64 to H68 are this entry's)

  • Question: since milestone 1 the trust flag is SPMe's own minimum salt ratio r_min, which needs an SPMe run. Milestone 5g found that the gate's cost hinges on how many designs in a pool are salt-starved, and its next steps asked for current density as a continuous axis and a dimensionless number that predicts the crossing without simulation. This step derives one and tests it against every committed label.
  • The predictor, fixed now (experiments/sand/run.py, r_ss): the steady state of the linear electrolyte problem under a uniform reaction in each electrode (the profile SPMe's leading-order correction relaxes to). With q = (1 - t+) i / F, effective diffusivity D_k = D_e(c0, T0) eps_k^b_k in each region, and zero flux at both collectors, the profile is piecewise quadratic-linear-quadratic, shifted so its porosity-weighted mean is c0. r_ss = min over discharge and charge (same current) of min c / c0, which is linear in current: r_ss = 1 - I / I_ss. D_e and t+ are evaluated at c0 and the set's initial temperature; nothing is fitted. A design is predicted suspect when r_ss <= 0.10 (milestone 2's flag threshold, unchanged).
  • Secondary predictor, no verdicts: r_t = 1 - (1 - r_ss)(1 - exp(-t_d / tau)), with tau the slowest mode's time constant (porosity-weighted L^2 / (pi^2 D_eff)) and t_d the nominal discharge time scaled by positive loading (Q_nom x eps_s,p L_p / its set's own, over the current).
  • Data, committed: the 19 conditions of milestones 5b to 5h (seven cells at 1x, 5g's six, 5h's six), 64 designs each, SPMe@100 (V0) and DFN@100. Labels as committed: suspect = SPMe returned nothing or whole-run r_min <= 0.10; mis-scored = milestone 1's label (SPMe score <= 0 or 25% below DFN@100), on 5e's pool (designs whose DFN finished). The predictor has seen none of these numbers; the shares and counts in this log have been read.
  • Data, fresh: three cells no milestone has used, ORegan2022, Prada2013 (LFP) and Ramadass2004 (SPMe fails at the baseline design in 5e's probe), at 0.25, 0.5, 1, 1.5, 2 and 3 times 48.7 A/m2, on 16 Sobol designs (scrambled, seed 7, not used before) plus the baseline design, SPMe (V0) and DFN for 2 cycles each, one fresh process per run. Simulation, mapping and copied degradation keys are 5g's, imported unchanged. Runs that fail or stop early are labels (SPMe) or dropped and counted (DFN), as before.
  • Amendment, before any fresh run returned a label: a baseline probe (SPMe and DFN for 2 cycles at 1x) found that ORegan2022 and Prada2013 (and Chen2020_composite and Xu2019, tried as replacements) fail inside 5b's design mapping on missing parameters (for example Bulk solvent concentration, which the mapping does not copy), so no run of theirs is a label. Ramadass2004 runs (DFN finishes, SPMe fails structurally, as in 5e's probe). The fresh sweep is therefore Ramadass2004 plus three committed cells on fresh designs and currents: Marquis2019, Mohtat2020 and NCA_Kim2011 (the cells whose committed suspect shares are lowest, so the sweep up to 3x can show a crossing), same rates, seed 7, 17 designs. H68's crossing test runs over these four cells (factor-2 misses on two of four refute it). Fresh here means designs and currents no milestone has run, and for three of the four cells not a fresh cell.
  • Second amendment, written after the committed verdicts (H64 to H67) were computed and before any fresh-sweep label was read (the bench was still running): the linear r_ss ranks the committed designs almost perfectly but sits below SPMe's r_min (at r_ss 0.1 the median SPMe r_min is 0.26), and the transient is not the cause (the discharge lasts at least 6 times the slowest diffusion time). D_e(c) rises as the salt empties in most sets, which a constant-D formula misses. The steady state with D_e(c) is still closed form through the Kirchhoff variable Phi(c) = int_0^c D_e: the flux equation is linear in Phi, so Phi has the piecewise profile above with eps^b in place of D_eff, and one bisection imposes mass conservation in c (r_kt in experiments/sand/run.py; t+ still at c0). On the committed data, seen while writing it, r_kt misclassifies 3 of 1280 designs. H69 (pre-registered for the fresh sweep only): the rule r_kt <= 0.10 misclassifies at most 2% of fresh designs, and the mean absolute difference between max(r_kt, 0) and max(SPMe r_min, 0) on designs where SPMe ran is at most 0.02. Refuted if misclassification is above 5% or the mean difference above 0.05.
  • H64 (rank): Spearman(r_ss, SPMe r_min) over committed designs where SPMe returned a run is at least 0.8 pooled, and at least 0.6 within at least 15 of the 19 conditions. Refuted if pooled below 0.6.
  • H65 (classify without simulation): pooled AUC of -r_ss for the suspect label is at least 0.90, and the fixed rule r_ss <= 0.10 misclassifies at most 15% of committed designs. Refuted if AUC below 0.80 or misclassification above 25%.
  • H66 (the gate's input): per condition, the predicted suspect share is within 0.15 of the observed share on at least 15 of 19 conditions. Refuted on fewer than 10.
  • H67 (what matters, mis-scoring): pooled AUC of -r_ss for the mis-scored label is at least 0.80 and within 0.05 of the AUC of SPMe's own r_min (the simulated flag, failures counted as r 0). Refuted if below 0.70.
  • H68 (fresh cells, continuous current): on the fresh sweep, pooled AUC of -r_ss for the suspect label (2-cycle SPMe) is at least 0.90, and for each fresh cell the baseline design's predicted crossing multiple (r_ss = 0.10) lies within a factor 1.5 of the bracket the sweep observes (last multiple not suspect, first suspect). Refuted if the AUC is below 0.80 or the crossing misses by more than a factor 2 on two of the three cells.
  • Also reported, no verdicts: Spearman with DFN's r_min, r_t's AUCs, per-cell I_ss for the baseline design, and the misclassified designs.
  • Caveats fixed now: the predictor ignores concentration dependence beyond c0, the non-uniform reaction (DFN's), the transient (except r_t) and the solid phase; the committed shares were read before the predictor was written, so H64 to H67 test a parameter-free formula on seen data, and only H68 is on unseen data; one PyBaMM version (26.10.1.1).
  • Script: experiments/sand/run.py; outcome logged above this entry.

2026-11-13 · Milestone 6a outcome: against measured discharges, swapping SPMe for DFN never moves capacity by more than 1.5 points while the parameter set is off by up to 4.3; SPMe's r_min does not order the gap across cells; the cell heats by 10 K at 2C, and once that is modelled DFN's apparent 2C win over SPMe shrinks from 1.5 to 0.3 points

  • Bench: 18 runs (SPM, SPMe, DFN x 6 conditions), none failed, 0.1 to 0.4 s each; measured files from pybamm-data v1.0.2, hash-checked by pybamm.DataLoader. Measured capacity to V_cut: Ecker2015 0.1610 Ah (1C), 0.1521 (5C); Ai2020 2.3323, 2.3077, 2.2788, 2.2258 Ah (0.1C to 2C).
  • H61 supported: SPMe is never closer to the measured capacity than DFN by more than 0.13 points (Ecker2015@5C, SPMe -2.62% against DFN -2.75%).
  • H62 mixed: Spearman(SPMe r_min, excess error) = -0.14 over the six. The two lowest r_min values tell opposite stories: Ecker2015@5C at r_min 0.42 has SPMe and DFN within 0.13 points, Ai2020@2C at 0.44 has them 1.50 points apart. As in milestone 5b, r_min ranks within a cell but its level does not carry across cells.
  • H63 supported: on all four conditions with SPMe r_min >= 0.5, |Q_SPMe - Q_DFN| (at most 0.06% of measured) is smaller than DFN's own error (0.88% to 4.26%). Where the flag trusts SPMe, the parameter set, not the model reduction, is what separates the model from the cell.
  • Prior work found after the run: research/energy-cell-dfn (2026-11-11) had run the same six comparisons on the same files, by voltage RMSE and with a lumped thermal model. This run's numbers reproduce its default-mesh ones to 0.1 mV (for example Ai2020@2C DFN 18.6 against 17.9 on its 4x mesh; lumped 46.3 against 46.3), from separate code. What is new here is the capacity framing with pre-registered tests tied to the trust flag (H61 to H63), and the post hoc items below; that project had left open whether the Ai cell was held at temperature.
  • Post hoc (after the verdicts, not pre-registered): (1) Ai2020 is +4.2% to +5.0% on capacity under every model at every rate, 0.1C included, so the set carries a rate-independent offset against this cell. Dividing it out (capacity at each rate over capacity at 0.1C), the measured 2C retention is 0.9543; isothermal SPM is +0.65 points, SPMe -0.60, DFN -1.98. (2) PyBaMM's lumped thermal model gives a peak temperature rise of 1.64, 4.06 and 10.37 K at 0.5C, 1C and 2C; the measured files (*_discharge_T.txt) give 1.57, 4.04 and 10.41 K. The cell was not isothermal. Whether the Ai2020 thermal parameters were fitted to these temperatures was not checked; if they were, the match is expected rather than independent. With lumped thermal the 2C retention errors are SPM +0.75, SPMe -0.17, DFN -0.47 points, the SPMe-DFN capacity gap falls from 1.50 to 0.32 points, and DFN's 2C voltage RMSE rises from 18.6 to 46.3 mV (SPMe 66.6). So DFN's isothermal 2C fit, the best number in either project, is a heating error cancelling the +4% offset. On Ecker2015@5C lumped thermal improves every model (DFN -2.75% to -1.78%, 85.6 to 57.9 mV).
  • Reading: on two commercial cells at up to 5C, the choice between SPMe and DFN moves delivered capacity by at most 1.5 points (0.3 once heating is modelled), while the published parameter set misses by up to 4.3 points and the thermal option moves the answer by up to 1.7. For the programme this bounds what DFN verification buys on mildly depleted cells (r_min 0.3 to 1): it is real but second order to parametrisation and temperature. The salt-depleted designs where SPMe fails outright (r_min near 0, milestones 1 to 5) are not reached by any measured curve here, so H4 (the design ranking against measured cells) is still open.
  • Caveats: default mesh only (energy-cell-dfn found Ecker2015@5C moves 15 mV between 1x and 4x meshes); two cells, discharge only; the parameter sets were built on these cells; the measured temperature is likely a surface reading, against the model's volume average.
  • Output: experiments/measured/bench.jsonl, bench_lumped.jsonl, results.txt, summary.json, measured.svg.

2026-11-13 · Milestone 6a: against measured discharges of two commercial cells, is DFN closer than SPMe, and does SPMe's own salt flag say where it departs from the measurement? (plan, written before the run; H61 to H63 are this entry's)

  • Question: every milestone so far scored SPMe against DFN. Milestone 6 (H4) asks whether the fidelity ranking holds against measured cells. No measured design sweep is reachable from this session, so this first step checks the three model forms against the measured constant-current discharges PyBaMM's data registry ships (pybamm-data v1.0.2, fetched through pybamm.DataLoader and checked against its SHA-256 sums): the Kokam SLPB 75106100 cell of Ecker et al. (2015) at 1C and 5C (digitised curves, about 30 points each), and the Enertech pouch cell of Ai et al. (2020) at 0.1C, 0.5C, 1C and 2C (1 s sampling).
  • Models and settings, fixed now: PyBaMM 26.10.1.1 SPM, SPMe and DFN with default options (isothermal, no degradation), the shipped Ecker2015 and Ai2020 parameter sets with their own initial concentrations, current = C-rate x the set's nominal capacity (0.15625 Ah and 2.28 Ah), model cut-off 2.5 V (Ecker2015) and 3.0 V (Ai2020). r_min is each run's minimum electrolyte concentration over time and space over the initial 1000 mol/m3.
  • Metrics: delivered capacity to a common cut-off V_cut (2.8 V Ecker2015, 3.05 V Ai2020, above every measured end voltage), as the relative error (Q_model - Q_meas)/Q_meas; voltage RMSE over the time both curves cover.
  • H61 (fidelity order holds against measurement): on every condition DFN's absolute capacity error is at most SPMe's plus 1 percentage point. Refuted if SPMe is closer by more than 2 points on any.
  • H62 (the flag points at the departure): SPMe's excess error, |err_SPMe| - |err_DFN|, is ordered by SPMe's r_min: Spearman(r_min, excess) <= -0.6 over the six conditions. Refuted if above 0. (Six points; a weak test, stated as such.)
  • H63 (where SPMe is trusted, parametrisation dominates): on conditions with SPMe r_min >= 0.5, |Q_SPMe - Q_DFN| is smaller than |Q_DFN - Q_meas| on at least two thirds of them. Refuted if on fewer than one third.
  • Also reported, no verdicts: SPM's errors, DFN r_min, voltage RMSE per model.
  • Caveats fixed now: both parameter sets were fitted or measured on these same cells (Ai2020's on these very discharges, as far as its paper reports), so this is a check of model form under the authors' own parametrisation, not an out-of-sample test; the models are isothermal and the cells are not; two cells, six conditions; one PyBaMM version.
  • Script: experiments/measured/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5h outcome: the band stop returns the DFN best on all six new conditions at no more than 1.07x all-DFN, but the iterate step it was built to fix also does, so the fix is insurance not shown to be needed on fresh data

  • Bench: 788 runs (64 Sobol seed-6 designs x SPMe V0 and DFN@100 x 6 conditions, plus 20 V1 re-solves), 3 workers, no memory kills. All six conditions passed the probe. On Ai2020@0.25x, 13 of 64 DFN runs failed in the first cycle (IDA_ERR_FAIL, minimum step size) and were dropped as the plan says, leaving 51 designs; every other DFN run reached 100 cycles.
  • H56 supported: the band answer is the pool's DFN best on all six (gap 0.0000).
  • H57 supported: band wall time over all-DFN 1.07 (Ai2020@0.75x), 0.72, 0.61, 0.57, 0.33, 0.70. The one above 1 is a cell where SPMe mis-scores 48 of 64 designs.
  • H58 refuted: two conditions had a pool median DFN/SPMe ratio over sound designs of at least 1.10 (Ai2020@0.75x 1.315; the others 1.00 to 1.05), and the iterate step reached the DFN best on both, as it did on all six. So the failure the band stop was built for (5g's Ai2020@0.5x, 3.2% short) did not recur on fresh designs, and the stop's need is not shown.
  • What the insurance cost: 9 more DFN runs than the iterate step on Ai2020@0.75x (60 against 51, wall time 1.07 against 0.93 of all-DFN), 11 more on Ai2020@0.25x (31 against 20; 0.72 against 0.51), 1 more on Ecker2015@0.5x, none on the other three.
  • H59 supported: rule recall 1.00 on Ai2020@0.75x (48 mis-scored), Ai2020@0.25x (17) and NCA_Kim2011@0.5x (16), 0.97 on OKane2022@1.5x (29 of 30; the missed design 57 has r_min 0.065, SPMe 28% below DFN, and DFN 3.7% below the pool best, so the answer was unaffected). Chen2020@0.5x and Ecker2015@0.5x had no mis-scored design.
  • H60 supported: Ai2020's suspect share is 0.06 at 0.25x (at most 0.31) and 0.53 at 0.75x (between 0.31 and 0.72). With 5g and 5f the share is 0.06, 0.31, 0.53, 0.72 at 0.25x, 0.5x, 0.75x, 1x: monotone in current on four different design draws.
  • Reading, across all 19 conditions now run (13 development, 6 fresh): the iterate step misses the DFN best on 1 (Ai2020@0.5x, 3.2%); the band stop misses on none, at a cost of 0 to 13 extra DFN runs per pool (up to 0.21 of all-DFN wall time). Whether that is worth it depends on how much a 3% miss costs a designer against a fifth more simulation time; neither answer step is shown to dominate. Current again moved SPMe's reliability more than the change of cell: at half current Chen2020 and Ecker2015 had no mis-scored design at all.
  • Output: experiments/band/probe.json, bench.jsonl, results.txt, summary.json, dev.txt, dev.json, band.svg.

2026-11-13 · Milestone 5h: does a gap-aware stop fix the answer step where SPMe under-scores sound designs? (plan, written before the run; H56 to H60 are this entry's)

  • Question: milestone 5g left one open problem. On Ai2020@0.5x SPMe under-scored almost every sound design (median 24% below DFN), so the iterate answer step compared a verified DFN score with biased-low SPMe scores and stopped 3.2% short of the pool's DFN best. 5g's own next step: keep verifying while an unverified design's SPMe score is within the observed SPMe-DFN gap of the verified best.
  • The band stop, fixed now: start from milestone 5e's verified set (rule unchanged). Let b be the verified design with the best DFN@100 and q the median DFN/SPMe ratio over verified sound designs (positive screen score and r_min > 0.1), floored at 1 (1 if none). While some unverified design with a positive screen score has score x q >= DFN(b), verify the one with the highest screen score, then recompute b and q. The answer is b, so it is always a verified design. Wall time: every SPMe run (V0 plus V1) plus every DFN run the rule and the stop make.
  • Seen before this entry (development, experiments/band/dev.txt): the stop was chosen on the 13 committed conditions (5g's six and the seven 1x cells) from four variants (median or max ratio; sound or all verified designs). The median-over-sound form returns the DFN best on all 13 (gap 0) and costs the same calls as the iterate step on 11; on Ai2020@0.5x it takes 47 calls against 34 (wall time 0.87 of all-DFN) and on Ai2020@1x 62 against 61. The max-ratio forms also reach the best but verify the whole pool on up to 7 conditions. So nothing below is new evidence about those 13.
  • New conditions, in this order, none used by any milestone: Ai2020 0.75x, Ai2020 0.25x, NCA_Kim2011 0.5x, Chen2020 0.5x, Ecker2015 0.5x, OKane2022 1.5x (multiples of milestone 5b's 48.7 A/m2). Low currents were chosen because SPMe's under-scoring appeared at Ai2020's lower current. A probe (baseline design, SPMe at V0 and DFN for 2 cycles) keeps each condition where both finish.
  • Designs: 64 Sobol designs (scrambled, seed 6, not used before) per kept condition; SPMe@100 at V0 and DFN@100 on every design, one fresh process per run, 3 at a time; V1 re-solves of every early stop; designs whose DFN does not reach 100 cycles are dropped and counted. Simulation, mapping, protocol and labels are 5g's (experiments/gate/run.py), imported unchanged.
  • H56 (answer): the band answer's DFN@100 is within 1% of the pool's DFN@100 best on every kept condition. Refuted if more than 2% below on any.
  • H57 (cost): the band procedure's wall time is at most 1.15 x all-DFN on every condition. Refuted if above 1.30 on any.
  • H58 (the problem recurs): on at least one condition where the pool's median DFN/SPMe ratio over sound designs is at least 1.10, 5g's iterate answer misses the DFN best by more than 1%. Refuted if it misses by at most 1% on every such condition; untestable if none has a ratio of 1.10. (If refuted, the band stop's need is not shown on fresh data, whatever H56 says.)
  • H59 (recall): on each condition with a mis-scored design, the 5e rule verifies at least 90% of them. Refuted if below 80% on any.
  • H60 (current orders Ai2020's suspect share): at 0.25x the share is at most 0.31 (5g's 0.5x) and at 0.75x it lies between 0.31 and 0.72 (the 1x share), each with 0.05 slack. Refuted if either misses by more than 0.10; between is mixed.
  • Also reported, no verdicts: calls and wall time of both answer steps, q at the stop, mis-scored counts, the pool's median ratio.
  • Caveats fixed now: the stop was read off the 13 development conditions; one PyBaMM version (26.10.1.1); 64 designs per condition; current is the only condition changed.
  • Script: experiments/band/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5g outcome: current, not the cell, decides how often SPMe breaks (Chen2020 25% to 81% at 2x); the registered gate picks wrong on 2 of 6 conditions but never costs more than 1.13x; the iterate answer misses by 3.2% where SPMe under-scores everything

  • Parallel work and numbering: this step was planned and run alongside milestone 5f (#15350, merged while this bench ran), which neither run saw. Both registered H46 to H50; this step's are renumbered H51 to H55 here with no other change to the plan's text, and the step is renamed 5g. Both used Sobol seed 5, so Ecker2015, Mohtat2020 and Ai2020 here run the same 64 designs as 5f's 1x benches: a paired comparison of current on identical designs, which neither plan foresaw.
  • Bench: 768 runs (64 Sobol seed-5 designs x SPMe V0 and DFN@100 x 6 conditions) plus 4 V1 re-solves. All six conditions passed the probe; every DFN run reached 100 cycles, so none was dropped. Ten Ai2020@0.5x DFN runs were killed for memory at 4 workers and re-run at 2 (not recorded as failures; their wall times, 28 to 34 s, were measured at 2-way concurrency, the other 54 at 4). Mohtat2020@2x had 4 early SPMe stops; V1 finished all 4 and none was mis-scored.
  • H55 supported: the suspect share moves with current on every cell. At 2x: OKane2022 0.18 to 0.81, Chen2020 0.25 to 0.81, Ecker2015 0.06 to 0.70, Marquis2019 0.00 to 0.22, Mohtat2020 0.00 to 0.02; Ai2020 at 0.5x falls from 0.72 to 0.31. At 2x OKane2022 and Chen2020 fail on the same 43 designs (OKane2022 is Chen2020's cell with SiOx and fitted degradation, which do not enter the first discharge's salt balance).
  • H51 refuted: the gate skipped SPMe on OKane2022@2x (7 of 8 suspect), Chen2020@2x (7) and Ecker2015@2x (5), and was wrong on OKane2022 (rule/all-DFN 0.94) and Ecker2015 (0.90); right on Chen2020 (1.07), Marquis2019@2x (0.78), Mohtat2020@2x (0.43) and Ai2020@0.5x (0.66). None was within 5%, so all six count. The cause: a structural SPMe failure costs under a second (median V0 time 0.9 s on OKane2022@2x against 27.4 s for DFN), so a pool full of failures makes SPMe cheap, not expensive. The suspect share alone is the wrong signal; the time ratio matters as much.
  • H52 supported: the gated wall time is 1.00 to 1.13 times the cheaper branch on every condition (worst Ecker2015@2x). Being wrong costs little because the two branches are close exactly where the gate is unsure.
  • H53 supported: the rule verified every mis-scored design on both conditions where the gate ran it and some design was mis-scored (Marquis2019@2x 10 of 10, Ai2020@0.5x 31 of 31). Recall was also 1.00 on the three skipped conditions, had the rule run.
  • H54 refuted: the gated answer is the DFN best on five conditions, but 3.2% short on Ai2020@0.5x (117.4 against 121.2 Wh/kg). There SPMe under-scores almost every design (median 24% below DFN, no failures), the DFN-best design sits 17% low at r_min 0.47, 42nd in the verify queue, and the rule stops at r_min 0.39 after three sound designs. The iterate step then compares a verified DFN score with SPMe scores that are now biased low, so the unverified best never leads. 5e's pre-registered answer misses there too (3.2%), and on Ecker2015@2x by 10.3%, Mohtat2020@2x 2.8% and Marquis2019@2x 0.4%, where the iterate answer reaches the best.
  • Paired with 5f's 1x runs on the same designs (after the verdicts): every design whose suspect status changed moved the way H55 predicted. Ecker2015: 39 designs became suspect at 2x and none recovered (share 0.09 to 0.70); Ai2020: 25 recovered at 0.5x and none broke (0.70 to 0.31); Mohtat2020: 1 became suspect (0.00 to 0.02). On Ai2020 5f's verified answer step returned the DFN best in all 30 draws at 1x; on the same designs at 0.5x it is 3.2% short, so 5f's reading that the answer step is settled holds at 1x only.
  • Extra, after the verdicts (post hoc, 13 conditions including the seven 1x cells): (1) a cost-aware gate that also runs DFN on design 0 and predicts rule/all-DFN as mean SPMe time of the first 8 over that DFN time plus the suspect share is right on all six new conditions and on 6 of 7 at 1x (wrong on Ai2020@1x, predicting 0.90 against 1.10). (2) Comparing like with like, verifying every unverified design whose SPMe score is at least the best verified design's, reaches the best on 12 of 13 (Ecker2015@2x 0.9%) but verifies all 64 designs on four conditions, so it is no cheaper than all-DFN where failures abound. (3) An affine map from SPMe to DFN fitted on the verified designs is worse (gaps up to 14.6% on Marquis2019@2x), because the verified designs are the salt-depleted ones, and the line does not extrapolate to the sound ones.
  • Relation to 5f's switch: 5f's pilot switch is cost-aware (its prediction adds the SPMe/DFN time ratio from 2 pilot DFN runs), close to this step's post hoc cost-aware gate; this step's registered gate used the suspect count alone, and its refutation is the argument for 5f's form. 5f's conclusion, run the rule every time, agrees with H52 here (at most 1.13x) at currents 5f did not test.
  • Reading: whether SPMe can be trusted is a property of the operating point as much as of the cell. Doubling the current turns a cell where SPMe is mostly right into one where it fails on four designs in five. The screen half of the rule kept full recall at every condition. The decision to skip SPMe is cheap to get wrong (at most 13% here), so a designer can run the rule by default. The open problem is the answer: an SPMe bias in either direction breaks a mixed-fidelity comparison, and the fixes tried so far are either expensive or worse. The next step should pre-register a stopping rule that keeps verifying while unverified designs' SPMe scores are within the observed SPMe-DFN gap of the verified best.
  • Output: experiments/gate/probe.json, bench.jsonl, results.txt, summary.json, gate.svg.

2026-11-13 · Milestone 5g: can the SPMe run itself say when to skip SPMe, and does the verified-answer rule hold at C-rates no number has been seen for? (plan, written before the run; H51 to H55 are this entry's)

  • Question: milestone 5e left two things. On the salt-limited cells (Ai2020, NCA_Kim2011) the two-part rule costs more wall time than running DFN on every design, so a designer needs to know from the cheap runs, early, when to skip SPMe; and the pre-registered answer step mixed fidelities, so the corrected one (verify the merged leader until it is a verified design) needs a test on data it was not read off. Salt depletion is driven by current, so this step moves to operating conditions no run has used: the same cells at a different current.
  • Seen before this entry (post hoc, on the seven committed 1x cells): the share of suspect designs (SPMe at default tolerances returns nothing, or its whole-run r_min <= 0.1) is 0.00 to 0.25 on the five cells where the rule is cheaper and 0.72 and 0.94 on Ai2020 and NCA_Kim2011; among the first 8 designs in Sobol order it is at most 1 of 8 on the first group and 6 and 8 of 8 on the second. The gate below was read off these numbers.
  • The gated procedure, fixed now: (G) run SPMe@100 at V0 on designs 0 to 7 in Sobol index order; if at least 4 of the 8 are suspect, stop using SPMe and run DFN@100 on the whole pool (answer: the DFN best; wall time: those 8 SPMe runs plus every DFN run). (R) Otherwise run milestone 5e's rule unchanged (V1 re-solve of early stops, failures first, then ascending r_min, stop after 3 consecutive sound designs) and then the iterate answer step: while the leader of the merged scores (DFN where verified, screen score elsewhere) is unverified, verify it; the answer is that leader. Wall time: every SPMe run (V0 plus V1) plus every DFN run the rule and the answer step make. Early stops are not suspect (milestone 5d: they are the solver's).
  • Conditions, in this order: OKane2022 at 2x the areal current density, Chen2020 2x, Marquis2019 2x, Ecker2015 2x, Mohtat2020 2x, Ai2020 0.5x (milestone 5b's 48.7 A/m2 is 1x; 2x is about a 2C rate on the OKane2022 cell). A probe (experiments/gate/run.py probe: the baseline design, SPMe at V0 and DFN for 2 cycles) keeps every condition where both finish both cycles. Mapping, protocol, voltage window, degradation options and copied keys are milestone 5b's; only the current is multiplied.
  • Designs: 64 Sobol designs (scrambled, seed 5, not used before) per kept condition; SPMe@100 at V0 and DFN@100 on every design, one fresh process per run, 4 at a time; V1 re-solves of every early stop. Designs whose DFN run does not reach 100 cycles are dropped and counted (5e's rule). Wall times are each run's own, measured under the same 4-way concurrency for both models.
  • Labels: mis-scored is milestone 1's (screen score 0 or more than 25% below DFN@100), on the score after the V1 re-solve.
  • H51 (gate decision): on each condition the gate picks the branch that is cheaper in measured wall time (rule with the iterate answer, against all-DFN); conditions where the two are within 5% do not count. Refuted if it picks wrong on 2 or more counted conditions; 1 is mixed; untestable if none counts.
  • H52 (gate cost): the gated wall time is at most 1.15 times the cheaper branch's on every condition. Refuted if above 1.30 on any.
  • H53 (recall at new currents): on each condition where the gate runs the rule and some design is mis-scored, the rule verifies at least 90% of the mis-scored designs. Refuted if below 80% on any.
  • H54 (answer): the gated answer's DFN@100 is within 1% of the pool's DFN@100 best on every condition. Refuted if more than 2% below on any.
  • H55 (current drives the suspect share): at 2x each cell's suspect share over its 64 designs is no lower than its committed 1x share minus 0.05 (1x: OKane2022 0.18, Chen2020 0.25, Marquis2019 0.00, Ecker2015 0.06, Mohtat2020 0.00); for Ai2020 at 0.5x it is no higher than 0.72 plus 0.05. Refuted if any condition misses by more than 0.10; between is mixed. (The pools differ, hence the margin.)
  • Also reported, no verdicts: each condition's mis-scored count, calls, rule/all-DFN wall-time ratio, the 5e pre-registered answer's gap beside the iterate one, and the gate applied post hoc to the seven 1x cells it was read off.
  • Caveats fixed now: one PyBaMM version (26.10.1.1); 64 designs per condition; the gate's 8 and 4 and the 0.1 flag are read off seven cells, not tuned on these; current is the only condition changed.
  • Script: experiments/gate/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5f outcome: reading the answer from verified designs returns the DFN best in all 120 draws, and the re-solve holds on fresh stops; the pilot switch misses on Ai2020, but the rule never costs more than 12% over DFN on everything

  • Bench: 515 runs (64 Sobol seed-5 designs x SPMe and DFN x 4 cells, plus 3 V1 re-solves), none killed, every DFN run reached 100 cycles, so no design was dropped. SPMe stopped early on 3 Mohtat2020 designs (cycles 8, 20, 76) and failed outright on 50 NCA_Kim2011 designs; mis-scored shares 0% (Mohtat2020), 91% (Ai2020), 80% (NCA_Kim2011), 0% (Ecker2015).
  • Fixed branches: rule against all-DFN wall time 185 against 442 s (Mohtat2020), 1393 against 1248 s (Ai2020, all-DFN cheaper by 11.6%, the only decisive cell where it wins), 953 against 968 s (NCA_Kim2011, within 10%), 461 against 949 s (Ecker2015).
  • H46 refuted: on Ai2020 the switch fires in 6 of 30 draws (20%). On the other two decisive cells it never fires, which is right (100%). The cause is the suspect cut-off: r* = 0.10 flags 70% of Ai2020's pool while the rule verifies 97%, because 13 of its 58 mis-scored designs have r_min between 0.10 and 0.32. The development replay had shown the same underestimate (0.72 against 0.95) and the plan disclosed it.
  • H47 mixed: median wall time 1.08x the cheaper branch on Mohtat2020, 1.12x on Ai2020, 1.03x on NCA_Kim2011 (where the switch fires in 97% of draws though the rule is 1.6% cheaper, so the wrong call costs little), 1.04x on Ecker2015. The overhead on benign cells is the 2 pilot DFN runs, which land on designs the rule would not have verified.
  • H48 supported: the returned design is the pool's DFN best in all 120 draws (gap 0), and so is the fixed rule branch's on all four cells. Verifying the leader until it is a verified design fixes 5e's Marquis2019 slip, and it cost 0 to 2 calls more than the queue.
  • H49 supported: V1 takes all 3 Mohtat2020 stops to 100 cycles, each within 0.2% of DFN@100 (gaps +0.001 to +0.002). Second fresh-design confirmation of 5d's reading after 5d's 6 of 6.
  • H50 supported: every draw that kept the rule verified every mis-scored design (recall 1.00 on Ai2020 and NCA_Kim2011; none on the other two).
  • Also reported: variant A (DFN on all 8 pilot designs) switches right in 80% of Ai2020 draws (median 1.02x) but costs 1.21x and 1.29x on the benign cells, as in the development replay.
  • Reading: the answer step and the re-solve are now settled on fresh data. The switch is not worth having as built: on these four cells, and on the seven of the development replay, the gap between the rule and all-DFN is never more than 12% when all-DFN wins, while the rule saves 49 to 64% of the all-DFN time on the six pools with few mis-scored designs (13% on Chen2020). A pilot that spends DFN runs costs 2 to 8% on those pools (this switch) or 10 to 29% (variant A). So the practical procedure is the rule with the verified answer step, run every time; a cell that is salt-limited across most of its design space loses at most about a tenth. A per-cell r* would fix H46 but needs DFN labels, which is variant A's cost.
  • Output: experiments/switch/dev.txt, dev.json, bench.jsonl, results.txt, summary.json, switch.svg.

2026-11-13 · Milestone 5f: can a pilot of 8 SPMe runs tell a designer, before the sweep, whether to run the rule or DFN on everything, and does reading the answer from verified designs return the DFN best? (plan, written before the run; H46 to H50 are this entry's)

  • Question: 5e left two fixes. Its answer step mixed verified DFN scores with biased SPMe ones (Marquis2019, 1.3% short), and on salt-limited cells (Ai2020, NCA_Kim2011) the rule cost 5 to 10% more wall time than running DFN on every design. A designer needs to choose the branch before paying for it.
  • The switch (fixed now): draw 8 designs at random from the pool and run SPMe@100 on them (V0, with 5e's V1 re-solve of stops). Run DFN@100 on the first 2 of those 8 in the rule's queue order (failures, then ascending r_min; they are at the front of the verify queue either way). Predicted share of all-DFN wall time = median SPMe time of the pilot's non-failed runs / mean DFN time of the 2 + the pilot's suspect share (failed, or r_min < 0.10) + 3/64. If it is 1 or more, run DFN on the other designs and return the best. Otherwise run SPMe on the rest and the 5e rule, with the 2 pilot DFN runs already verified (they still count toward, or reset, the run of 3 sound designs).
  • The answer step (fixed now): while the design with the best score (DFN where verified, screen score elsewhere) is unverified, verify it; return it. This is 5e's post hoc "iterate" variant (gap 0 on all seven cells there).
  • How the constants were chosen, disclosed: a development replay (experiments/switch/run.py dev, dev.txt) on the seven committed cells, which is post hoc. A first variant that ran DFN on all 8 pilot designs paid 11 to 28% overhead on benign cells (its DFN runs land on sound designs), and a first version of the queue that skipped pre-verified designs without counting them lost OKane2022 recall (0.87) and the pick (6.1% short); both were changed before this plan. With the frozen switch, the replay gives a median wall time of 1.00 to 1.10 times the cheaper fixed branch on all seven cells and a pick gap of 0 in every draw. The r* = 0.10 suspect share tracked the rule's verified share on five cells (0.18 against 0.17 on OKane2022, 0.25 against 0.23 on Chen2020) and underestimated it on Ai2020 (0.72 against 0.95).
  • Cells and designs: Mohtat2020 (the cell with solver stops, so the re-solve gets a second test), Ai2020 and NCA_Kim2011 (salt-limited, where all-DFN won in 5e), Ecker2015 (benign). 64 scrambled Sobol designs with seed 5 (not used before), SPMe@100 at V0 and DFN@100 on every design, V1 on every stop, 5b's mapping, protocol and degradation keys, one fresh process per run. Each draw is replayed from the bench: 30 pilot draws per cell (random.Random(s).sample, s = 0 to 29); wall time is summed per-run seconds, as in 5e.
  • Fixed branches: rule (5e's queue from scratch plus the new answer step) and all-DFN. The cheaper branch is the one with less wall time; a cell is decisive when the two differ by more than 10%.
  • H46 (switch): on each decisive cell the switch picks the cheaper branch in at least 80% of draws. Refuted if below 60% on any; untestable if no cell is decisive.
  • H47 (cost): the switched procedure's median wall time is at most 1.10 times the cheaper branch on each cell. Refuted if above 1.20 on any.
  • H48 (answer): in every draw on every cell the returned design's DFN@100 is within 1% of the pool's DFN best. Refuted if any draw is more than 2% short.
  • H49 (re-solve, 5e's H43 again): every stop V1 finishes scores within 25% of DFN@100. Refuted if more than one does not; untestable without stops.
  • H50 (recall): in draws that keep the rule, at least 90% of mis-scored designs are DFN-verified on each cell. Refuted if below 80% in any draw.
  • Also reported, no verdicts: the switched share, calls, and the variant that runs DFN on all 8 pilot designs.
  • Caveats fixed now: one PyBaMM version (26.10.1.1); 64 designs per cell; four cells, three of them seen in 5b and 5c on other designs, so this tests fresh designs more than fresh cells; the 25% label and the run of 3 are inherited.
  • Script: experiments/switch/run.py; outcome logged above this entry.

2026-11-13 · Milestone 5e outcome: on two new cells the rule catches every mis-scored design (9 of 9 on Chen2020) for 6 to 23% of the pool in DFN runs; its answer step was wrong once, because it compared verified DFN scores with unverified SPMe ones

  • Probe: Ramadass2004's baseline SPMe run fails (every step infeasible at the first cycle; its DFN salt reaches 0), Prada2013 and ORegan2022 fail on missing keys as in 5c, so the plan's order chose Marquis2019 and Chen2020. Bench: 256 runs (64 Sobol seed-4 designs x SPMe and DFN x 2 cells), none killed, every DFN run reached 100 cycles (median 9.3 and 6.2 s), no SPMe run stopped early, so no V1 re-solve was needed. Chen2020's SPMe failed outright on 3 designs (every step infeasible), Marquis2019's on none.
  • H42 supported, on one cell: Chen2020 has 9 mis-scored designs (14%), 3 failures and 6 salt-depleted, and the rule verifies all 9. Marquis2019 has none (SPMe within 0.4% of DFN at the median, 5.6% at worst; r_min 0.30 to 0.83), so it does not count.
  • H43 untestable: no early stops on either cell.
  • H44 mixed: on Chen2020 the pick is the DFN best (gap 0). On Marquis2019 it is 1.3% below it (196.8 against 199.5 Wh/kg). The cause is the answer step, not the screen: SPMe ranks Marquis2019's DFN-best design first, and the rule verified it (it has the lowest r_min but one), but SPMe scores its ten best designs 1 to 6% above DFN (median gap over all 64 is 0.4%), so an unverified design's SPMe score (201.4) beat the verified DFN-best (199.5) and was confirmed instead.
  • H45 supported: calls 4 on Marquis2019 (0 mis-scored + 4) and 15 on Chen2020 (9 + 6), 6% and 23% of the pool; with every SPMe run, 45% and 87% of the all-DFN wall time (on Chen2020 a DFN run costs only 1.6 SPMe runs).
  • Chen2020's DFN-best design is salt-depleted (r_min 0.09) and SPMe scores it 23% low, just inside the 25% label, ranking it 16th of 64; the top 5 by SPMe all sit 6% or more below the best. The bottom-up queue reaches it because its r_min is low, which a top-k SPMe shortlist would not.
  • Extra, after the verdicts: two answer steps that do not mix fidelities. Returning the best DFN score among the designs already verified (no extra call) gives gap 0 on both new cells and on 4 of the 5 replayed cells (NCA_Kim2011 0.2%). Verifying the merged leader until it is a verified design gives gap 0 on all 7 cells at 0 to 2 more calls (Marquis2019 6, NCA_Kim2011 58 of 64).
  • Post hoc replay on the five cells the rule was built on (no verdicts): recall 1.00 on the four with mis-scored designs; DFN calls 17%, 8%, 95%, 5% and 88% of the pool (OKane2022, Ecker2015, Ai2020, Mohtat2020, NCA_Kim2011); pick gap 0 except NCA_Kim2011 (0.2%). On the salt-limited Ai2020 and NCA_Kim2011 the rule costs more wall time than running DFN on everything (110%, 105%), because nearly every design is mis-scored and SPMe was run as well.
  • Reading: on fresh designs and a cell it was not built on, the screen part of the rule held: it found every design SPMe got wrong, including the DFN-best, at the cost the plan allowed. The pre-registered answer step was the weak part: it compares a verified DFN score with SPMe scores carrying a few per cent of bias. Read the answer from verified designs only, or keep verifying the leader. When most of the pool is mis-scored (Ai2020, NCA_Kim2011), skip SPMe and run DFN.
  • Output: experiments/rule/probe.json, bench.jsonl, results.txt, summary.json, rule.svg.

2026-11-13 · Milestone 5e: does the two-part rule from 5c and 5d (re-solve early stops tightly; DFN-verify failures and low-r_min designs bottom-up) hold on cells no number has been seen for, and does it return the DFN-best design? (plan, written before the run; H42 to H45 are this entry's)

  • Question: milestones 5c and 5d built the rule post hoc on five cells. A designer needs to know whether it holds on a new cell, and whether, used as a screen, it hands back the design full DFN would have picked. This step fixes the rule now and runs it on new parameter sets and fresh designs.
  • Cells: probe (experiments/rule/run.py probe, baseline design, SPMe and DFN for 2 cycles) the candidates Ramadass2004, Marquis2019, Chen2020, Prada2013, ORegan2022 in that order, and take the first two whose SPMe and DFN runs both succeed (Chen2020 is late in the order because OKane2022 is built on it). Prada2013 and ORegan2022 failed 5c's probe on missing keys and are kept only as fallbacks under the same mapping. Milestone 5b's design mapping, protocol, areal current density and copied degradation keys, unchanged.
  • Designs: 64 Sobol designs (scrambled, seed 4, not used before) per chosen cell; SPMe@100 at V0 (IDAKLU defaults) and DFN@100 at V0 on every design, one fresh process per run.
  • The rule, applied design by design from the SPMe output only: (1) a run that returns 1 to 99 cycles (stop) is re-solved once at V1 (IDAKLU rtol 1e-6, atol 1e-8); if V1 returns 100 cycles its score and r_min replace V0's, otherwise it counts as a failure. (2) A run that returns no cycle, or a stop V1 cannot finish (failure), gets screen score 0 and goes to the front of the verify queue. (3) The rest are queued by ascending r_min (ties by index). DFN-verify in queue order and stop after 3 consecutive sound designs (SPMe score within 25% of DFN@100, milestone 1's label). (4) The pick is the design with the highest score, using DFN@100 where verified and the screen score elsewhere; if it was not verified, one more DFN call confirms it. Calls = verified designs + that confirmation.
  • Labels: a design is mis-scored when its screen score (after step 1) is 0 or more than 25% below DFN@100. Designs whose DFN@100 run does not return 100 cycles are dropped and counted.
  • H42 (recall): on each chosen cell the rule DFN-verifies at least 90% of mis-scored designs. Refuted if below 80% on either; between is mixed. A cell with no mis-scored design is reported and does not count.
  • H43 (re-solve): every stop V1 finishes scores within 25% of DFN@100. Refuted if more than one does not; untestable on a cell with no stop.
  • H44 (pick): the pick's DFN@100 is within 1% of the pool's DFN@100 best on each cell. Refuted if more than 2% below on either.
  • H45 (cost): calls are at most the number of mis-scored designs plus 8 on each cell. Refuted if more than mis-scored plus 16 on either.
  • Also reported, no verdicts: calls and wall time as a share of all-DFN; the same rule replayed post hoc on the five committed cells (OKane2022 cycles, Ecker2015, Ai2020, Mohtat2020, NCA_Kim2011, using 5d's V1 runs for stops), labelled post hoc because the rule was built on them.
  • Caveats fixed now: one PyBaMM version (26.10.1.1); 64 designs per cell; the stop-after-3 constant and the 25% label are inherited, not tuned here.
  • Script: experiments/rule/run.py; outcome logged above this entry.

2026-11-12 · Milestone 5d outcome: SPMe's early stops are the solver's (tight tolerances finish all 6, each within 0.3% of DFN); its outright failures are SPMe's (salt concentration below zero in 59 of 61, no setting rescues a usable score)

  • Bench: 455 SPMe runs (67 census designs and 24 controls x 5 variants) plus 67 one-cycle diagnostics. V0 reproduces every committed cycle count (91 of 91). None killed. A first report keyed designs by (set, index) and merged OKane2022 index 1 of the fresh bench (a failure) with index 1 of the cycles bench (a control); the rows now carry their bench and the report keys on it, no run repeated.
  • H38 supported: V1 (IDAKLU rtol 1e-6, atol 1e-8) and V3 (Casadi "safe", same tolerances) take all 6 Mohtat2020 stops to 100 cycles; V4 (mesh doubled) takes 4; V2 (more Newton iterations and convergence failures allowed) takes none and stops each at the same cycle as V0. So it is the error-test tolerance, not the nonlinear solve, that ends these runs.
  • H39 supported: the 6 rescued designs score within 0.3% of DFN@100 (gaps -0.000 to +0.003); none is mis-scored. So on Mohtat2020 every mis-score came from the solver setting: the other 58 designs were already within 2.3% per cycle in 5c (only 8 of them were re-run here, as controls).
  • H40 supported: no variant gives a usable score to any of the 61 outright failures. V3 returns 100 cycles on 4 NCA_Kim2011 designs and V1 on one of those, but three score 0 (no energy after cycle 1) and one 30.6 against DFN's 70.4 Wh/kg; all four stay mis-scored. The diagnostic puts SPMe's first-discharge salt concentration below zero on 59 of 61 (median -0.08 of initial, low -0.15), and on 57 the charge step comes back empty: the state the discharge ends in has left the reduced model's domain, so no feasible step follows and PyBaMM discards the finished cycle.
  • H41 supported: all 6 stops keep positive salt in the first discharge (0.65 to 0.89 of initial).
  • Controls: V1 and V3 move completed scores by at most 2.2%, V4 by up to 8.2% (one NCA_Kim2011 design at r_min -0.06), V2 not at all; no control breaks. Extra, after the verdicts: on Mohtat2020's controls tight tolerances halve SPMe's median distance to DFN@100 (1.01% to 0.50%); on NCA_Kim2011 (1.03 to 1.08%) and OKane2022 (5.46 to 5.43%) they change nothing. DFN was not re-solved at tight tolerance.
  • Two failures do not fit: OKane2022 cycles design 16 and NCA_Kim2011 design 2 keep positive salt (0.05, 0.16) and finish their first charge, then fail later under every variant. Not diagnosed further.
  • Reading: 5c's two kinds of mis-score are two different things. An SPMe run that stops early with healthy salt is PyBaMM's default tolerance (rtol 1e-4) losing the step; re-solve it once at rtol 1e-6 (about 2.4x the run time, 3.8 against 1.6 s) and it scores like DFN. A run that returns nothing has driven its linearised salt concentration negative in the first discharge; that is SPMe outside its validity, no solver setting helps, and it goes to DFN with the salt-depleted ones. So the practical two-part rule becomes: re-solve stops tightly; send failures and low-r_min designs to DFN bottom-up. 5c's refutations on Mohtat2020 (H33, H34, H37) stand as registered, but their cause was the solver setting, not the flag.
  • Output: experiments/solver/census.json, diag.jsonl, bench.jsonl, results.txt, summary.json, solver.svg.

2026-11-12 · Milestone 5d: are SPMe's solver stops and outright failures numerical (a solver setting removes them) or structural (SPMe's electrolyte leaves its domain)? (plan, written before the run; H38 to H41 are this entry's)

  • Question: milestone 5c found that every SPMe mis-score on Mohtat2020 was a run that stopped part-way, and that 49 of NCA_Kim2011's 52 were runs that returned nothing; 12 OKane2022 runs (milestones 2 and 5a) also returned nothing. 5c called these "numerical failures, not model error". If a tighter or more robust solver finishes them, a designer should re-solve before flagging; if no setting can, the failure is SPMe's, and the flag is the right response. This step tests which, design by design.
  • Seen before this entry (one design, by hand): NCA_Kim2011 design 0 runs 1 cycle under SPMe (0.42 Wh) but fails at 2 or more. Its first discharge drives SPMe's electrolyte concentration to -97 mol/m3 before the 2.7 V cut-off; the charge step then comes back empty (infeasible at its initial state), so the second cycle has no feasible step and PyBaMM raises, discarding the finished cycle. That suggests a structural cause on NCA_Kim2011; the hypotheses below test it on every design.
  • Census (experiments/solver/run.py census, fixed now): every SPMe run on the committed benches (cycles, fresh, transfer, calibrate) that returned no cycle (fail: OKane2022 12, NCA_Kim2011 49) or fewer than 100 (stop: Mohtat2020 6). Controls: the first 8 designs by index on Mohtat2020, NCA_Kim2011 and OKane2022 (cycles bench) whose SPMe run completed, 24 in all.
  • Variants, SPMe for 100 cycles, milestone 5b's mapping, protocol and degradation options unchanged: V0 IDAKLU defaults (rtol 1e-4, atol 1e-6; reproduces the committed runs), V1 IDAKLU rtol 1e-6 and atol 1e-8, V2 IDAKLU with a robust nonlinear solve (max_nonlinear_iterations 200, max_convergence_failures 1000, max_error_test_failures 100), V3 CasadiSolver mode "safe" at rtol 1e-6 and atol 1e-8, V4 IDAKLU defaults with every mesh dimension doubled. One fresh process per run, 455 runs.
  • Diagnostic: for every census design, one SPMe cycle at V0, recording the first discharge's unclipped minimum c_e / c_e0 (ce1_min_ratio), its energy and termination, and whether the charge step came back empty.
  • A design is rescued when some variant V1 to V4 returns all 100 cycles; its score is that variant's SPMe@100 (the first such variant in V1 to V4 order), compared with the committed DFN@100; untrusted is milestone 1's label (score 0 or more than 25% below DFN).
  • H38 (stops are numerical): some variant brings at least 4 of Mohtat2020's 6 stops to 100 cycles. Refuted if none brings more than 1; between is mixed.
  • H39 (rescued stops are sound): no rescued stop is untrusted. Refuted if more than one is; one is mixed.
  • H40 (failures are structural): no variant brings more than 10% of the 61 failures to 100 cycles, and at least 90% of them have ce1_min_ratio < 0. Refuted otherwise.
  • H41 (stops are not structural): at least 90% of the 6 stops have ce1_min_ratio >= 0. Refuted otherwise.
  • Also reported, no verdicts: each variant's counts by group and set; each control's largest score change under each variant (a variant that moves sound runs by more than 1% would make rescued scores suspect) and whether any control breaks; whether V0 reproduces each committed cycle count.
  • Caveats fixed now: one PyBaMM version (26.10.1.1); four solver settings and one mesh change, not an exhaustive search; the controls are 24 designs.
  • Script: experiments/solver/run.py; outcome logged above this entry.

2026-11-12 · Milestone 5c outcome: SPMe mis-scores designs in two ways, and the salt flag sees only one; flag runs that stop early, then verify bottom-up in r_min order with no calibration

  • Bench: 256 PyBaMM runs, 64 Sobol (seed 3) designs x SPMe and DFN x Mohtat2020 (X, by the registered fallback) and NCA_Kim2011 (X2, the amendment). Every DFN run reached 100 cycles (median 8.1 s and 19.1 s). SPMe stopped early on 6 of 64 Mohtat2020 designs (at cycles 3 to 90) and failed outright on 49 of 64 NCA_Kim2011 designs (SolverError). On Mohtat2020 design 19, rerun by hand: IDA's corrector failed to converge mid-discharge and PyBaMM returned the 3 finished cycles as a normal solution.
  • Mis-scored (untrusted): Mohtat2020 6 of 64, exactly the 6 early stops. Up to the stop their per-cycle discharge energy is within 3.7% of DFN's (within 2.5% before the last cycle; the 58 designs that finish are within 2.3% on every cycle), and their r_min is 0.65 to 0.89, far from depletion. NCA_Kim2011 52 of 64: 49 outright failures (r_min 0 by the code's convention) and 3 salt-depleted runs.
  • Primary verdicts (X = Mohtat2020): H33 refuted (B_3 recall 0.00 on Mohtat2020; 1.00 on OKane2022 and Ai2020), H34 refuted (C_8 median recall 0.17 on Mohtat2020), H35 mixed (B_3 dominates C_8 on OKane2022, 42 vs 58 calls, and Ai2020, 61 vs 63; on Mohtat2020 neither dominates), H36 supported in letter (9.4% misclassified, but by flagging nothing: recall 0), H37 refuted (AUC 0.486).
  • X2 (NCA_Kim2011): H33 to H37 all supported (B_3 recall 1.00 in 56 calls against C_8's 59; F misclassifies 9.4%; AUC 0.921). Most of that comes from the failure convention: 49 of the 52 mis-scored designs are SPMe runs that produced nothing.
  • Also reported: C_8's cut-off is noisy (OKane2022 10th-percentile recall 0.85, below 0.8 in 7.9% of draws) and its random calibration runs land mostly on sound designs, so it costs more calls than B_3 on every set where both reach full recall: 58 vs 42 (OKane2022), 63 vs 61 (Ai2020), 12 vs 4 (Ecker2015), 59 vs 56 (NCA_Kim2011). The fixed cut-off F still misses 23% on Ai2020. Ecker2015's single mis-scored design is caught by every strategy.
  • Extra, after the verdicts (section G): among SPMe runs that reach cycle 100, the mis-scored designs are all salt-depleted and r_min ranks them at AUC 0.995 (OKane2022, 21 of 244), 0.995 (Ai2020), 1.000 (Ecker2015, 1) and 1.000 (NCA_Kim2011, 3 of 15); Mohtat2020 has none. Flagging every run that stops short as well gives B_3 recall 1.00 on all five sets at 16%, 95%, 6%, 14% and 88% of the pool (the mis-scored share is 13%, 89%, 2%, 9%, 81%), always fewer calls than C_8 (23%, 98%, 19%, 27%, 92%).
  • Reading: H2's hope of one physical cut-off is gone (5b), and a random calibration sample is a poor fix: it is noisy and pays for sound designs. Two checks, both free from the SPMe run itself, cover every mis-scored design across five cells: did the run finish, and how low did its salt go. Verify DFN from the most-depleted design up and stop after three sound ones in a row. The registered label counted solver stops as mis-scoring; that is how a search sees them (score 0), but they are numerical failures, not model error, and they announce themselves.
  • Output: experiments/calibrate/bench.jsonl, probe.json, results.txt, summary.json, calibrate.svg.

2026-11-12 · Milestone 5c: milestone 5b found the trust flag's ranking transfers but its cut-off does not; how should a practitioner set the cut-off on a new cell, and how many DFN runs does that cost? (plan, written before the run; H33 to H37 are this entry's)

  • Question: on a new cell the r_min ranking holds (AUC 0.995 on Ai2020) but OKane2022's cut-off of 0.07 does not (Ai2020's own best is 0.33). A designer then has two options: calibrate a cut-off from a few DFN runs on random designs, or skip the cut-off and DFN-verify designs in ascending r_min order until a run of trusted ones. This step compares them on the committed sets and on one new parameter set no number has been seen for.
  • Sets: OKane2022 (256 designs, milestones 2 and 5a pooled), Ai2020 and Ecker2015 (64 each, milestone 5b), and a new set X, 64 Sobol designs (scrambled, seed 3), SPMe and DFN for 100 cycles (128 runs), milestone 5b's mapping, protocol, areal current density and copied degradation keys unchanged. Ecker2015 (1 untrusted design) is reported but cannot decide a verdict.
  • Choosing X, fixed now: probe the baseline design for 2 cycles under SPMe and DFN on Mohtat2020, NCA_Kim2011, Prada2013 and ORegan2022, in that order (all PyBaMM 26.10.1.1 sets; Chen2020 is skipped because OKane2022 is built on it). X is the first whose both runs succeed and whose SPMe r_min lies in 0.05 to 0.45 (neither deep in depletion like Ai2020 nor outside it like Ecker2015); if none qualifies, the first whose runs succeed.
  • Label, unchanged: untrusted = SPMe@100 score 0 or more than 25% below DFN@100. r_min = the minimum of SPMe's 100-cycle run. Every cost is counted in DFN@100 calls; SPMe has already run on every design.
  • Strategies. F: verify every design with r_min <= 0.07 (5b's t*). C_k: DFN-run k designs drawn uniformly at random, set the cut-off to the largest value in 0.00 to 1.00 (step 0.01) that minimises misclassification on those k (largest, so ties favour recall), then verify the other designs at or below it; 1000 draws (seed 0), k in 4, 8, 16, 32. B_s: verify designs in ascending r_min (ties by index) and stop after s consecutive trusted ones, s in 1, 2, 3, 5, 8. Metrics: recall (untrusted designs that got a DFN run over all untrusted) and DFN calls as a share of the pool. Headline settings C_8 and B_3.
  • H33 (bottom-up works without calibration): B_3's recall is at least 0.90 on OKane2022, Ai2020 and X. Refuted below 0.80 on any. X is the out-of-sample test: OKane2022's and Ai2020's AUCs (0.997, 0.995) were seen before this entry, so passing there is expected.
  • H34 (a small random calibration works): C_8's median recall is at least 0.90 on each of those three sets. Refuted below 0.80 on any.
  • H35 (bottom-up dominates): on each of those sets B_3's recall is at least C_8's median and its calls at most C_8's median. Refuted if C_8's median has higher recall and fewer calls than B_3 on any set; otherwise mixed.
  • H36 (H29 on a third cell): F misclassifies at most 20% of X's designs. Refuted above 20%.
  • H37 (H30 on a third cell): the AUC of -r_min for untrusted on X is at least 0.90. Refuted below 0.80; inconclusive if X has fewer than 3 untrusted or 3 trusted designs.
  • Also reported, no verdicts: every k and s; X's own best cut-off; the 2-cycle r_min's AUC on X; whether each strategy DFN-verifies the DFN-best design when it is untrusted. Caveats fixed now: 64 designs on three of the four sets; one protocol; cells are design-space variants of each set, not the published cells.
  • Script: experiments/calibrate/run.py; outcome logged above this entry.
  • Amendment after the probe, before any bench run: no candidate's baseline SPMe r_min fell in 0.05 to 0.45 (Mohtat2020 0.82, NCA_Kim2011 -0.03; Prada2013 and ORegan2022 fail on missing parameters), so the rule's fallback makes X = Mohtat2020, which may have too few untrusted designs to decide H37. NCA_Kim2011 is added as a second new set X2 (same 64 designs, same runs), reported with H33 to H37 applied to it separately; the primary verdicts stay as registered (X = Mohtat2020).

2026-11-12 · Milestone 5b outcome: the trust flag's ranking transfers to Ecker2015 and Ai2020 but its cut-off does not; "short SPMe beats long SPMe" is an OKane2022 effect; cheap-first screens still beat GP-EI on both sets

  • Bench: 384 PyBaMM runs, 64 designs x 3 models x 2 sets, all DFN and SPMe runs reached 100 cycles; on Ai2020 the plain SPM stopped after 1 cycle on 13 of 64 designs (score 0, kept). DFN@100 best / median: Ecker2015 336.7 / 291.5 Wh/kg, Ai2020 113.0 / 84.8 (stack level, 5% inactive rule, so Ecker2015 sits above its published cell). SPMe r_min median: Ecker2015 0.37, Ai2020 0.00 (SPMe's c_e goes slightly negative on Ai2020, 10th percentile -0.01). Untrusted: Ecker2015 1 of 64, Ai2020 57 of 64 (OKane2022 33 of 256).
  • t* on OKane2022's 256 designs is 0.07 (misclassification 0.023, AUC 0.997).
  • H29 refuted: t* misclassifies 1.6% on Ecker2015 but 20.3% on Ai2020 (bar 20%). Ai2020's own best cut-off is 0.33 (1.6%): at its current density SPMe is more than 25% low on designs whose salt never fully depletes in SPMe.
  • H30: Ai2020 supported (AUC 0.995, 2-cycle r_min also 0.995); Ecker2015 inconclusive (1 untrusted design, which r_min ranks first: AUC 1.000).
  • H31 refuted on both: Spearman(SPMe@10) - Spearman(SPMe@100) = -0.012 (CI -0.034 to 0.004) on Ecker2015 and -0.111 (-0.259 to 0.020) on Ai2020. On OKane2022 it was +0.09; there the 10-cycle advantage comes from the set, not from SPMe.
  • H32 supported: the 9 methods' median T1 on pools of 32 order like OKane2022's at Spearman 0.733 (Ecker2015) and 0.700 (Ai2020), the second exactly at the bar.
  • Pools of 32: GP-EI 105.7 s (Ecker2015) and 130.3 s (Ai2020). Faster, p < 0.001 unless noted: Ecker2015 DFN@2 screen 61.4, SPMe@2 68.7, SPMe@10 70.0, SPM@2 71.3, cheap-start MF-UCB 56.5 (fastest); Ai2020 SPMe@10 51.4 (p 0.038, fastest), DFN@2 53.2, SPMe@2 62.0, cheap-start 71.0. On Ai2020 the plain SPM ranks DFN at Spearman 0.32 and both SPM screens are slower than GP-EI (207.4 and 171.1 s).
  • Extra, after the verdicts (section G): worst ratio to the fastest method over the three sets at pools of 32: SPMe@2 screen 1.22, DFN@2 screen 1.29, SPMe@10 1.40, cheap-start MF-UCB 1.71, GP-EI 3.73, SPM@2 4.03, SPMe@100 4.33.
  • Reading: what transfers is the order, not the numbers. SPMe's own minimum salt ratio still ranks the designs it mis-scores almost perfectly on a cell that depletes (Ai2020), but the cut-off has to be set per cell, so H2's claim that one asymptotic threshold serves every parameter set is refuted. A practitioner should rank by r_min and verify from the bottom, or calibrate the cut-off with a few DFN runs. The cheapest robust screen across all three sets is a 2-cycle run (SPMe or DFN), within 1.3x of the fastest method everywhere; SPM, fine on OKane2022 and Ecker2015, fails on the salt-limited Ai2020 cell.
  • Output: experiments/transfer/bench.jsonl, cost.json, probe.json, results.txt, summary.json, transfer.svg.

2026-11-12 · Milestone 5b: do the trust flag and the short-SPMe screen transfer to two other parameter sets, Ecker2015 and Ai2020? (plan, written before the run; H29 to H32 are this entry's)

  • Question: every result so far is on one parameter set (OKane2022, Chen 2020's NMC811/graphite-SiOx cell). The proposal's H2 asks whether the trust test's threshold, picked on OKane2022, transfers to other chemistries without refitting; milestone 5a left that open. This step also asks whether the short-SPMe screen and the ranking of search methods transfer.
  • Sets: Ecker2015 (Kokam SLPB 75106100; PyBaMM's positive OCP is labelled NCO, corrected from "NMC" after the run, description only) and Ai2020 (Enertech LCO/graphite pouch), as packaged in PyBaMM 26.10.1.1, the two the proposal names for H2. Chen2020 is skipped: OKane2022 is built on it, so it would test degradation parameters, not transport.
  • Design mapping, unchanged from milestone 2 (energy-cell's cell.py): positive thickness 50 to 150 um, both porosities 0.20 to 0.40, negative thickness from the set's own n/p thickness ratio times 0.9 to 1.3, active fraction 1 - porosity - 0.05, stack mass with each set's densities. Three per-set changes, fixed now: (1) the current is set so the areal current density equals the OKane2022 cell's (5 A over 0.1027 m2 = 48.7 A/m2; Ecker2015 0.418 A, Ai2020 3.97 A over its 34 parallel layers, mass multiplied by the layer count); (2) the voltage window is each set's own cut-offs (Ecker2015 2.5 to 4.2 V, Ai2020 3.0 to 4.2 V); (3) degradation parameters a set lacks are copied from OKane2022 (Ecker2015: initial SEI on cracks; Ai2020: the six lithium-plating parameters), so the same SEI and plating options run. The 5% inactive rule replaces each set's own inactive fraction (Ecker2015's positive has about 30%), so the cells are design-space variants of each set, not the published cells; disclosed.
  • Probe, seen before this entry: on the baseline design, Ecker2015 DFN@100 runs in 17 s and SPMe's r_min is 0.46; Ai2020 DFN@100 runs in 21 s and SPMe's r_min is about 0 (DFN's 0.05), with SPMe's 2-cycle energy 0.96 Wh against DFN's 5.26 Wh. So Ai2020 sits deep in salt depletion at this current density and Ecker2015 well outside it.
  • Data: 64 new designs (scrambled Sobol, seed 2), the same on both sets; SPM, SPMe and DFN, 100 cycles, one run each, per-cycle r = min c_e / c_e0 recorded; 384 runs. Baseline costs per set as milestone 2 (n = 2, 10, 30, 100, median of 3).
  • Label, as milestone 1: untrusted = SPMe@100 score 0 or more than 25% below DFN@100. r_min = the minimum over SPMe's 100-cycle run (milestone 2 found r set in the first discharge).
  • H29 (H2 as registered): the threshold t* minimising misclassification of untrusted by r_min <= t on OKane2022's 256 designs (milestones 2 and 5a, grid 0.00 to 0.50 step 0.01, ties to the smallest) misclassifies at most 20% of designs on each of Ecker2015 and Ai2020. Refuted if above 20% on either.
  • H30 (H1 transfers): ROC AUC of -r_min for untrusted is at least 0.90 on each set. Refuted below 0.80 on either; inconclusive if a set has fewer than 3 untrusted or 3 trusted designs.
  • H31 (short beats long): on each set, Spearman(SPMe@10, DFN@100) exceeds Spearman(SPMe@100, DFN@100) with the 95% bootstrap interval of the difference (2000 resamples, seed 0) above 0. Refuted if the point difference is at or below 0 on either set.
  • H32 (method ranking): 9 frozen methods (GP-EI at DFN@100; the seven whole-pool screens SPM@2, SPM@100, DFN@2, SPMe@2, SPMe@10, SPMe@30, SPMe@100; cheap-start co-kriging MF-UCB over DFN@2), replayed on 30 pools of 32 designs per set under that set's baseline costs (milestone 4's T1 rule, 1% target). The Spearman between the 9 methods' median T1 on OKane2022 (5a's fresh designs, pools of 32) and on each set is at least 0.7. Refuted below 0.5 on either; between is inconclusive.
  • Also reported, no verdicts: each set's own best threshold (H2's "within a factor of 2" of t*, which is undefined if t* is 0); the r_min distribution; fail counts; Spearman of every cell against DFN@100; the fastest method per set. Caveats fixed now: 64 designs per set; pools of 32 out of 64 overlap heavily, so p-values overstate independence; two sets, both graphite negatives.
  • Script: experiments/transfer/run.py; outcome logged above this entry.

2026-11-12 · Milestone 5a outcome: on 128 fresh designs the short SPMe screen holds (123 s against GP-EI's 220 s on pools of 64) and the method ranking transfers (Spearman 0.92); the cheap-start search beats GP-EI everywhere but trails the best screen on small pools

  • Bench: 384 PyBaMM runs (Sobol seed 1; nearest seed-0 design at normalised distance 0.07 to 0.34, median 0.18). SPMe fails 5 of 128, SPM and DFN none. DFN@100 best 163.5 and median 128.5 Wh/kg (seed 0: 162.3, 128.8). Two DFN children were killed by the session's memory limit at 4 workers; they were dropped and rerun at 2 workers (run.py now refuses to record an exit -9 as a model failure).
  • Reproduction: the seed-0 replay in the same script gives milestone 4b's and part 2b's medians exactly (GP-EI 220.4, SPMe@10 122.9, cheap-start MF-UCB 144.0 and 173.9 s).
  • H25 supported: SPMe@10 screen on pools of 64, median T1 122.9 s against GP-EI 220.4 (p = 2.2e-6) and the SPM@2 screen 205.0 (p = 0.0008).
  • H26 supported: Spearman with DFN@100, SPMe@10 0.668 against SPMe@100 0.575; difference 0.093 (95% CI 0.045 to 0.154). SPMe ranks the fresh DFN-best design 2nd at 10 cycles and 48th at 100 (seed 0: 1st and 41st).
  • H27 refuted: cheap-start MF-UCB over DFN@2 beats GP-EI at every size (62.4 / 89.6 / 123.6 / 140.6 s against 147.0 / 195.9 / 220.4 / 232.7, p <= 0.0032), but is 1.36 x the best screen at 16 (DFN@2, 46.0 s) and 1.71 x at 32 (SPMe@2, 52.5 s); 1.18 x at 64 and 0.94 x at 96, where it is the fastest method.
  • H28 supported: the 15 methods' median T1 on pools of 64 correlate at Spearman 0.924 between seed-0 and fresh designs.
  • Extra, after the verdicts (section C): the worst ratio of each method's median to the fastest method's, over the four pool sizes. SPMe@2 screen 1.37 (seed 0: 1.34), SPMe@10 1.40 (1.40), DFN@2 1.44 (1.46), SPM@100 1.58 (1.81), cheap-start MF-UCB over DFN@2 1.71 (1.72); GP-EI 3.73; SPMe@100 8.68. No single method is fastest at every size on either set, and the fastest per size moved (fresh: DFN@2 at 16, SPMe@2 at 32 and 64, cheap-start MF-UCB at 96).
  • Reading: what parts 2b and 4b found after the fact survives new designs on the same parameter set. A 2- or 10-cycle SPMe screen stays within 1.4 x of the best method at every pool size, and SPMe's short run ranks DFN's long run better than its own long run does. The cheap-start search is the safe choice only for large pools. Transfer to other parameter sets (H2, milestone 5b) is untested.
  • Output: experiments/fresh/bench.jsonl, results.txt, summary.json, fresh.svg.

2026-11-12 · Milestone 5a: do the short-SPMe screen and the cheap-start search, both found post hoc, hold on 128 fresh designs? (plan, written before the run; H25 to H28 are this entry's)

  • Question: parts 2b and 4b each ended on a post-hoc winner, a plain whole-pool SPMe@10 screen (122.9 s median T1 on pools of 64, faster than every milestone-4 method) and co-kriging MF-UCB over DFN@2 started from 10 low-rung runs (tied with the best screen at every pool size). Both were picked after seeing the 128 designs they were scored on. This step tests them, unchanged, on designs nobody has looked at.
  • Data: 128 new designs, scrambled Sobol with seed 1 (milestone 2 used seed 0) over the same energy-cell bounds, parameter set (OKane2022 via energy_cell.cell), protocol and code path (cycles/run.py's simulate, 100 cycles, one run per design and model, SPM, SPMe and DFN). Costs are milestone 2's cycles/cost.json (cost A), so only the designs change. Nearest-neighbour distance from each fresh design to the seed-0 set is reported. Same pools rule (30 seeds, random.Random(s).sample), 1% target, 16 / 32 / 64 / 96 designs.
  • Methods, all frozen as committed: GP-EI at DFN@100; whole-pool screens SPM@2, SPM@100, DFN@2, SPMe@2, SPMe@10, SPMe@30, SPMe@100; the four planned co-kriging variants and their four cheap-start versions (mfbo/run.py, no retuning). 15 methods.
  • H25 (short SPMe screen): on pools of 64, the SPMe@10 screen's median T1 is below GP-EI's and below the SPM@2 screen's, paired Wilcoxon p < 0.05 for each. Refuted if its median is at or above either.
  • H26 (short beats long): over the 128 fresh designs, Spearman(SPMe@10, DFN@100) exceeds Spearman(SPMe@100, DFN@100), with the 95% bootstrap interval of the difference (2000 resamples, seed 0) above 0. Refuted if the point difference is at or below 0.
  • H27 (cheap start): cheap-start MF-UCB over DFN@2 has median T1 below GP-EI's at every pool size (p < 0.05 each) and at most 1.2 x the best of the seven screens' medians at every pool size. Refuted if either part fails at any size.
  • H28 (ranking transfers): the Spearman correlation between the 15 methods' median T1 on pools of 64, seed-0 designs against fresh designs (both recomputed by this script), is at least 0.7. Refuted below 0.5; between is inconclusive.
  • Also reported, no verdicts: rank of the fresh DFN-best design under each SPMe and SPM screen; the r_min distribution; the fail counts per model. Caveats fixed now: one parameter set and one protocol, so this tests fresh designs, not transfer (H2 stays open for milestone 5b); pools overlap, so p-values overstate independence; costs are one machine's baseline times.
  • Script: experiments/fresh/run.py; outcome logged above this entry.

2026-11-12 · Milestone 3 outcome (theory, part 2b): SPMe's error follows -ln of its own minimum salt ratio, but that neither plans nor repairs the search; post hoc, a plain 10-cycle SPMe screen is the fastest yet on pools of 64 and 96 (exploratory)

  • Rerun check: 128 SPMe 100-cycle runs reproduce bench.jsonl per-cycle energies exactly (max relative difference 0), the same 7 failures, r_min within 5e-7.
  • H21 supported: 5-fold CV RMSE on SPMe@100, f ~ a + b s + beta g: g_log 11.34, g_quad 12.31, g_flag 16.80, none 21.27 Wh/kg (log / none 0.53). The four registered forms rank the same way at 2, 10 and 30 cycles. g_eta (extra) 13.25.
  • H22 refuted: location model from 16-design pilots, E[R] / observed mean R on pools of 64: SPMe@2 2.64, SPMe@10 9.07, SPMe@30 1.04, SPMe@100 0.71 (2 of 4 within 2x). The location-free model on the same pilots: 2.30, 7.44, 0.85, 0.59. Residual sd after the location is about 7 Wh/kg against a 1% tolerance of about 1.6.
  • H23 refuted: online g_log correction over SPMe@100, median T1 528.1 s against SPMe@100 + flag 417.8 s (p = 0.0001; median 12 against 7.5 DFN calls). With no feature the online rule is the plain screen (699.5 s).
  • H24 supported by its bar, empty in substance: online over SPMe@2 has median T1 129.4 s against SPM@2's 168.2 s (p = 0.038), but every feature and none give 129.4 s, because the target is found inside the 4 warm-up calls. The win is the plain SPMe@2 screen, which milestone 4 never ran.
  • Extra, post hoc (section E), plain whole-pool screens, median T1 at 16 / 32 / 64 / 96: SPMe@2 38.5 / 52.5 / 129.4 / 230.9 s; SPMe@10 49.1 / 73.7 / 122.9 / 172.1 s; SPMe@30 75.4 / 89.7 / 424.2 / 648.6 s. At 64, SPMe@10 against SPM@2, SPM@100, DFN@2 and GP-EI: p = 0.0005, 5e-5, 1e-4, 7e-6 (all faster). SPMe@30 is significantly slower than all of them.
  • Extra, post hoc: the DFN-best design (j = 12, r = 0.074) is ranked 8 / 1 / 27 / 41 by SPMe at 2 / 10 / 30 / 100 cycles. Without it, mean DFN calls on pools of 64: SPMe@10 1.10, SPMe@2 1.13, DFN@2 1.13, DFN@10 1.30, SPMe@30 1.60, SPMe@100 2.07, SPM@100 3.90, SPM@2 4.67. r is set in the first discharge (median 0.297 and 10th percentile 0.038 at every cycle count).
  • Reading: the physics says where SPMe errs (salt-depleted designs, in a -ln r shape), but the residual left over is too large to plan from, and a 4-point online fit cannot use it. A practitioner gets more from a short SPMe run than from correcting a long one. Next: pre-register the short-SPMe screens on fresh designs and other parameter sets, and explain why SPMe's 10-cycle ranking tracks DFN's 100-cycle ranking.
  • Output: experiments/location/results.txt, summary.json, location.svg, spme_cycles.jsonl; THEORY.md part 2b.

2026-11-12 · Milestone 3 (theory, part 2b): can SPMe's own salt-depletion output say where its error falls, well enough to plan the DFN budget and to correct the screen? (plan, written before the run; H21 to H24 are this entry's)

  • Question: part 2a found that no independent-noise model predicts SPMe's screening cost (it under-predicts SPMe@30 and SPMe@100 by 3.6x and 4.4x), because SPMe's large residuals sit on particular designs, and asked for the residual's location from the physics. Here the location is modelled from SPMe's own solution and tested three ways: as a fit, as a planner, and as a correction to the screen.
  • Mechanism (to write out in THEORY.md, part 2b; a scaling argument, not a theorem): in PyBaMM 26.10's SPMe the concentration overpotential is chi RT/F times the difference of the x-averages of log c_e over the two electrodes (electrolyte_conductivity.Composite, log clipped at a small tolerance), with one reaction rate for the whole electrode. As the cheap solution's minimum salt ratio r = min c_e / c_e0 falls to zero, that term grows like -ln r and pulls the voltage to the 2.5 V cut-off early. The DFN has the same log, but its reaction moves away from the depleted region, so its voltage does not follow ln of the minimum. So SPMe's extra energy loss, and hence its affine residual e = f - (a s + b), should scale with g_log(r) = -ln max(r, 0.01), not with the asymptotic order (1 - r)^2 of the expansion's correction.
  • Data: cached scores (experiments/cycles/bench.jsonl, cost.json, milestone 4's 30 pools of 64). One new PyBaMM pass: SPMe, 100 cycles, on the same 128 designs, same protocol and code path as cycles/run.py, recording r_min per cycle (and the most negative x-averaged concentration overpotential per cycle) so that SPMe@n's feature comes from its own first n cycles; its per-cycle energies must reproduce bench.jsonl (check reported). The 7 designs whose SPMe run fails have r = 0 by convention (clipped to 0.01).
  • Features, fixed now: g_log = -ln max(r, 0.01) (primary); g_quad = (1 - r)^2; g_flag = 1[r <= 0.1] (milestone 1's flag); g_eta = -min eta_c in volts (extra, no verdict).
  • H21 (form): on SPMe@100 over all 128 designs, 5-fold cross-validated RMSE (folds fixed by random.Random(0)) of the regression f ~ a + b s + beta g: g_log beats g_quad and g_flag, and is at most 0.7 of the regression with no g. Refuted if g_quad or g_flag is lower than g_log. Not blind: part 1's H13 already found Spearman(e, r) = -0.82.
  • H22 (planning): the location model e = beta g_log + N(0, sigma0^2), with a, b, beta, sigma0 fitted on a pilot of 16 random designs (20 pilots, median prediction), gives E[R] by part 2a's quadrature with per-design means f - beta g_log. On pools of 64, within a factor of 2 of the observed mean R on at least 3 of the 4 SPMe cells (2, 10, 30, 100 cycles). Refuted if 2 or fewer. Same convention as part 2a: the formula sees the pool's true f; only the residual model is fitted on the pilot.
  • H23 (corrected screen, SPMe@100): online corrected screen-then-verify: screen the whole pool, verify in descending s for the first 4 DFN@100 calls, then refit f ~ a + b s + beta g_log by least squares on the verified designs after every call and verify the unverified design with the largest prediction. On pools of 64 under milestone 4's costs, median T1 below SPMe@100 + flag's (417.8 s), paired Wilcoxon p < 0.05. Refuted if its median T1 is higher.
  • H24 (corrected screen, cheap rung): the same online correction over SPMe@2 (with its 2-cycle r) has median T1 at most the SPM@2 screen's 168.2 s on pools of 64. Refuted if above 1.2 x 168.2 s.
  • Also reported, no verdicts: the same online rule with g_quad, g_flag and no g (ablations) on every SPMe cell; GP-EI at DFN@100 as reference (220.4 s); the pool sweep 16, 32, 64, 96 for the best corrected cell. Caveats fixed now: pools overlap, so p-values overstate independence; H21's form was suggested by H13's correlation; one parameter set.
  • Script: experiments/location/run.py; outcome logged above this entry.

2026-11-12 · Milestone 4b outcome: co-kriging BO as planned loses to GP-EI at every pool size, because its 5 random full-model starts cost more than whole screens; started from cheap runs instead, it keeps pace with the best screen everywhere (exploratory)

  • References reproduce milestone 4 exactly on pools of 64 (GP-EI 220.4 s, SPM@2 screen 168.2, SPM@100 153.2, DFN@2 159.6), so the replay and its costs are the same.
  • H18 refuted: co-kriging with augmented EI over SPM@2 has median T1 240.3 s against GP-EI's 220.4 s on pools of 64 (p = 0.25). It needs 9.5 DFN@100 calls to GP-EI's 9; its 27 SPM@2 calls cost about 9 s.
  • H19 refuted: the best planned variant at 64, MF-UCB over DFN@2 (204.6 s, p = 0.23 against GP-EI), takes 267.1 s at 96 (1.21 x GP-EI, bar 1.1) and 157.1 s at 16 (3.4 x the DFN@2 screen's 46.0, bar 2.0). No planned variant beats GP-EI significantly at any pool size, and all four are significantly slower at 96 (p 0.002 to 0.035).
  • H20 supported: charging each design its own measured time (DFN 19 to 67 s a design in the benchmark) keeps the order of the 8 methods at Spearman 0.90 against baseline-cost charging. Every method gets slower (GP-EI 220 to 259 s) and the SPM@2 screen loses its significant lead over GP-EI (p = 0.34); SPM@100 and DFN@2 screens keep theirs.
  • Diagnosis: the planned start puts 5 random designs through DFN@100 (122.5 s) before the low rung can say anything, more than half of the best screen's whole T1 on pools of 64. The low-rung calls are cheap (under 25 s a search); the cost is in DFN calls, 7 to 11 for co-kriging against 3 to 6 for a screen.
  • Extra, not in the plan, chosen after seeing the above (so exploratory): the same four searches started from 10 random low-rung runs and DFN@100 on the best 2. All four beat GP-EI at 16, 32 and 64 (p <= 0.005), and MF-UCB over DFN@2 at 96 too (173.9 against 220.4 s, p = 0.0003). Against the best whole-pool screen at each size, MF-UCB over DFN@2 with the cheap start is 38.0 / 90.3 / 144.0 / 173.9 s against 46.0 / 67.6 / 153.2 / 199.3 s (wins 18 / 13 / 19 / 18 of 30, p 0.19 / 0.40 / 0.047 / 0.052): a tie with the best screen at each size, while no single screen is best at every size. The rung matters: with SPM@2 as the cheap rung the cheap-start searches are slower than the DFN@2 screen at 16 and 32 designs (wins 8 to 10 of 30, p 0.009 to 0.06). The cost split on pools of 64 (median calls x baseline cost): planned MF-UCB 183.7 s of DFN@100 and 19.5 s of DFN@2, cheap start 122.5 and 21.5 s. Measured against H19's bars it would pass (0.79 x GP-EI at 96, 0.83 x the best screen at 16), but the start was chosen post hoc and its two numbers (10, 2) were not tuned or varied, so this needs a pre-registered test on fresh designs (milestone 5's other parameter sets are the natural place).
  • Reading: in a pool replay the cheap rung pays off only if it is allowed to pick the first full-model runs; spending the first DFN budget at random throws away what made screens win. For a practitioner: start a multi-fidelity search with a handful of 2-cycle DFN runs, not with random full runs.
  • Output: experiments/mfbo/results.txt, summary.json, mfbo.svg.

2026-11-12 · Milestone 4b: does a co-kriging search that picks design and fidelity each step keep the screens' small-pool lead and GP-EI's large-pool one? (plan, written before the run; H18 to H20 are this entry's)

  • Question: milestone 4 found that whole-pool screening with a cheap rung (SPM@2, DFN@2) beats GP-EI on DFN@100 on pools of 16 to 64 but loses by 96, because screening pays per candidate. The proposal's evaluation asks for a two-fidelity co-kriging BO (Kennedy and O'Hagan) as the multi-fidelity baseline; this step runs it, with two published fidelity-selection rules, on the cached benchmark (no new PyBaMM runs).
  • Model: autoregressive co-kriging, f_h(x) = rho f_l(x) + delta(x), independent GPs (squared-exponential, isotropic, inputs scaled to [0, 1]) for f_l and delta, constant means per fidelity, signal variance profiled out, length scales, rho and the delta variance ratio by grid maximum likelihood, refit every 5 observations. Low rung SPM@2 or DFN@2, high rung DFN@100. Start: the same 5 random designs as GP-EI at DFN@100, plus those 5 at the low rung.
  • Rules: (i) augmented EI (Huang, Allen, Notz and Miller 2006): EI of f_h at x times, for a low-rung query, the posterior correlation of f_l(x) and f_h(x) and the cost ratio c_h / c_l; the (design, rung) pair with the largest value is run. (ii) MF-UCB after Kandasamy et al. (2016): pick x by the upper confidence bound of f_h (beta_t = 0.2 d log 2t, their practical setting); run it at the low rung if sqrt(beta_t) times the posterior sd of f_l(x) exceeds gamma = sqrt(c_l / c_h) times the fitted delta sd, else at DFN@100.
  • Replay: as milestone 4 (same random.Random(s).sample pools, 30 seeds, T1 = charged seconds until a design within 1% of the pool's best DFN@100 has been run at DFN@100), at pool sizes 16, 32, 64, 96. References re-run in the same script: GP-EI at DFN@100 and the SPM@2, SPM@100 and DFN@2 whole-pool screens. A search stops once it hits the 1% target (T1 does not depend on what comes after).
  • Costs: (A) each evaluation charged the cell's median baseline fresh-run cost (experiments/cycles/cost.json), as milestone 4; (B) each design charged its own cost, cost_base(cell) x seconds_j(model) / median over designs of seconds(model), from the 100-cycle benchmark timings (bench.jsonl, run three at a time, so the ratio, not the level, is used). DFN designs range 19 to 67 s there.
  • H18: on pools of 64, co-kriging with augmented EI and SPM@2 as the low rung has lower median T1 than GP-EI at DFN@100 (220 s in milestone 4), paired Wilcoxon p < 0.05. Refuted if its median T1 is higher than GP-EI's.
  • H19 (the envelope): the better of the four co-kriging variants (2 rules x 2 low rungs), chosen once on pools of 64 under cost A, has median T1 at most GP-EI's on pools of 96 and at most 1.5 times the best whole-pool screen's on pools of 16. Refuted if more than 10% above GP-EI at 96 or more than 2 times the best screen at 16.
  • H20 (cost heterogeneity): under cost B the order of the methods' median T1 on pools of 64 agrees with cost A's at Spearman >= 0.8. Refuted below 0.6.
  • Also reported: the 95% bootstrap interval of the median, DFN@100 and low-rung calls to T1, and the paired Wilcoxon p of every method against GP-EI. Caveats fixed now: pools share designs, so p-values overstate independence; the grid of hyperparameters is coarse; the pool replay is not a continuous search.
  • Plan change before the outcome run (logged before it): a 2-seed smoke test put the fitted rho at the bottom of the grid (0.6) and the low-rung length scale at its top (0.8), and with 40 DFN@100 points the co-kriging mean predicted held-out designs worse than plain GP (RMSE 5.4 against 2.9 Wh/kg). DFN@100 keeps about 60% of early-cycle energy, so rho below 0.6 is physical. The grid is widened to rho 0.2 to 1.2, length scales up to 1.6, delta variance ratio down to 0.005; the check then gives 7.1 against 11.8 Wh/kg at 10 points and 3.1 against 2.9 at 40 (SPM@2 low rung, 10 splits). Hypotheses unchanged; the smoke-test T1 values (2 seeds) were seen.
  • Script: experiments/mfbo/run.py; outcome logged above this entry.

2026-11-12 · Milestone 3 outcome (theory, part 2a): an independent-noise model plans screen against GP-EI right on 14 of 16 pool sizes, but cannot rank SPMe, whose residual sits on particular designs

  • Proposition written out with proof in THEORY.md (part 2a): with independent residuals, E[R] = 1 + the sum over designs outside tolerance of the chance each outscores every design inside it; exact for Gaussian residuals by one-dimensional quadrature. Unit-checked against a closed form, Monte Carlo and the random-order limit (tests/test_average.py).
  • H15 refuted: with sigma from the whole space, E[R] against the observed mean calls on pools of 64 has Spearman 0.51 over the 11 cells, within 2x on 7 of 11 (bars 0.8 and 8). It predicts about 10 calls for every SPMe cell; observed 1.0 (SPMe@10) to 14.0 (SPMe@100).
  • Extra, no verdict: sigma from part 1's top set ranks the cells at Spearman 0.86 (within 2x still 7 of 11); it under-predicts SPMe@30 and SPMe@100 by 3.6x and 4.4x.
  • H17 refuted: the design-independent resampled residual (model B) predicts 10.4 calls for SPMe@100 against 14.0 observed (ratio 0.74, registered bar for refutation within 1.5x). DFN@10 and DFN@30 are also over-predicted by more than 1.5x (2.2, 1.7), so the "B within 2x for SPM and DFN" half fails too.
  • H16 supported: simulated median T1 = N c_s + c_h median R under the Gaussian model calls screen against GP-EI right on 14 of 16 (screen, N) pairs, against 8 of 16 for part 1's worst-case corollary; median relative error in T1 0.24. Misses: SPM@2 and DFN@2 at N = 96 (predicted wins, observed losses). Optimistic for SPM@2 throughout (70 against 168 s at 64).
  • Reading: for screens whose residual is roughly design-independent, sigma near the top and the crowding of the top 1% plan the DFN budget; for SPMe the location of the large residuals (on the best designs at 100 cycles, below them at 10) decides the cost, so part 2b should derive where SPMe errs from the expansion, not how much.
  • Output: experiments/average/results.txt, summary.json, average.svg; THEORY.md part 2a.

2026-11-12 · Milestone 3 (theory, part 2a): does an average-case noise model predict screen-then-verify calls where the worst-case bound failed? (plan, written before the run; H15 to H17 are this entry's)

  • Question: part 1's worst-case corollary (H14) called screen against GP-EI right on only 8 of 16 pool sizes, because one large residual widens its band for every design. Here the screen's affine residual is treated as noise. Proposition (to prove in THEORY.md): if the affine-mapped screen is s' = f + e with e independent across designs and density g, and T is the set of designs within tolerance, then exactly E[R] = 1 + sum over x not in T of P(s'_x > max over y in T of s'_y), and for Gaussian e with sd sigma that probability is the one-dimensional integral of phi((t - f_x)/sigma)/sigma times the product over y in T of Phi((t - f_y)/sigma). Ranking only needs sigma relative to the spacing of f near the top, so sigma / (density of f in the top few percent) is the screen's average-case cost.
  • Data: cached only (experiments/cycles/bench.jsonl, cost.json, milestone 4's pools), no new PyBaMM runs. Same 11 screen cells and target DFN@100 as part 1, tau = 1%.
  • Residual (fixed now): least-squares affine fit of f on s over all 128 designs, e = f - (a s + b); the primary sigma is RMS(e) over the 128, failures (s = 0) included. Extras, no verdicts: sigma from the fit on part 1's top set S_q, and a robust sigma (1.4826 x MAD).
  • Models: G, Gaussian e with the primary sigma (exact E[R] by quadrature); B, e drawn with replacement from the cell's own 128 residuals, independent of the design (2000 Monte Carlo draws per pool). B keeps the residual's distribution and drops its link to the design; observed R keeps both.
  • H15 (the noise model predicts calls): on milestone 4's 30 pools of 64, model G's mean E[R] over the pools against the observed mean R, over the 11 cells: Spearman >= 0.8 and within a factor of 2 on at least 8 of 11. Refuted if Spearman < 0.6 or fewer than 6 within a factor of 2.
  • H16 (planning): predicted median T1 = N c_s + c_h x median R, with R simulated under G on 2000 pools of N drawn from the 128, against GP-EI's observed median T1 at each N, for H14's 16 (screen, N) pairs (SPM@2, SPM@100, DFN@2, DFN@10 at N = 16, 32, 64, 96). Supported if at least 13 of 16 win/lose calls are right, refuted if 10 or fewer (H14's bar). Also reported against H14's fixed 220.4 s. Not blind: the pools come from the same 128 designs the sweep used, and the sweep's medians were in milestone 4's outcome.
  • H17 (design-linked residual): for SPMe@100 the independent-residual model B under-predicts the observed mean R on pools of 64 by at least a factor of 2, because SPMe's residual is largest on the designs DFN scores highest (salt depletion in thick, high-energy designs, H13); for SPM@100 and every DFN cell B is within a factor of 2. Refuted if B for SPMe@100 is within a factor of 1.5 of observed. Also reported: Spearman(e, f) per cell.
  • Script: experiments/average/run.py; outcome logged above this entry. Part 2b (the salt-depletion residual from the SPMe expansion) stays open.

2026-11-11 · Milestone 3 outcome (theory, part 1): affine error is free, the residual is what costs DFN calls; SPMe's residual is salt depletion

  • Theorem written out with proof in THEORY.md: if the screen matches the target up to an affine map with worst residual kappa, every design screened ahead of the best is within 2 kappa of it, the DFN calls to 1% are bounded by the designs in that band, and a whole-pool screen costs at most c_h + N (c_s + p c_h).
  • C1: no violation on 11 cells x 30 pools (330 checks), plus 200 random instances in tests/test_theory.py.
  • H11 supported: across the 11 screen cells, the top-25% residual kappa_q ranks median DFN@100 calls at Spearman 0.72; the raw median |s - f| at -0.07. The whole-pool kappa_all gives only 0.53 (single outliers dominate it).
  • H12 supported: on the 121 designs SPMe completes, kappa_all is 11.0 Wh/kg for SPM@100 against 42.8 for SPMe@100 (ratio 0.26), with similar raw errors (7.1 against 9.5).
  • H13 supported: SPMe@100's affine residual has Spearman -0.82 with its own r_min (lower salt, larger under-score); SPM@100's +0.26. Residual RMS 17.7 against 4.4 Wh/kg. This is the quantitative form of "the SPMe correction hurts ranking": its design-dependent error is the salt-depletion term.
  • H14 refuted: the worst-case corollary calls screen against GP-EI right on 8 of 16 (screen, pool-size) pairs (bar 13): it calls SPM screens losers at every pool size (band fraction 0.53, N* about 14) though they win up to 64. Right on DFN@10 at all four sizes. A sup-norm residual is too pessimistic for planning; an average-case model is next.
  • Also: SPMe@10 has median R = 1 and top-1 regret 0 on the 128, though SPMe@100 needs 19: the SPMe residual grows with cycling (milestone 2), and the DFN-best design is outside SPMe@100's top 25%, so kappa_q is not a valid bound for that cell.
  • Next (part 2): derive the salt-depletion residual from the SPMe expansion, and an average-case R(N) to replace H14's worst-case corollary.
  • Output: experiments/theory/results.txt, summary.json, theory.svg; THEORY.md.

2026-11-11 · Milestone 3 (theory, part 1): what kind of screen error costs DFN calls, and when does whole-pool screening lose? (plan, written before the run; H11 to H14 are this entry's)

  • Question: milestones 2 and 4 found that SPM, whose raw error against DFN is as large as SPMe's (median +7.1 against -8.7 Wh/kg), screens far better, and that every whole-pool screen loses to GP-EI as the pool grows. This step states the theory that should explain both and tests it on the cached data (experiments/cycles/bench.jsonl, no new PyBaMM runs).
  • Theorem (to write out in THEORY.md): pool P, target f (DFN@100), screen s, x* = argmax f, screen-then-verify runs f in descending s. For any u >= 0 and c, let kappa = max over S of |u s(x) - c - f(x)|, where S contains x* and every x with s(x) >= s(x*). Then every design screened ahead of x* has f(x) >= f* - 2 kappa, so (i) top-1 regret <= 2 kappa, (ii) the number R of DFN@100 calls to reach (1 - tau) f* is at most 1 + #{x in P : f* - 2 kappa <= f(x) < (1 - tau) f*}, and (iii) R = 1 when 2 kappa <= tau f*. The best kappa is an affine Chebyshev fit (a linear programme). Corollary: T1 = N c_s + R c_h <= c_h + N (c_s + p(2 kappa) c_h), with p(w) the fraction of the pool within w of the top but outside tolerance, so a screen has an effective cost per candidate c_s + p c_h and loses to a search needing m DFN calls once N > (m - 1) c_h / (c_s + p c_h).
  • Diagnostics computed: kappa over all designs (kappa_all) and over S_q = the top q = 25% by s together with the top 25% by f (kappa_q; the theorem applies when x* is in the screen's top 25%, reported), for the 11 (model, cycles) screen cells other than DFN@100, on the 128 and on each pool; raw error = median |s - f|; R per cell over the 30 pools of 64 of milestone 4 (same random.Random(s).sample pools).
  • C1 (a check, not a hypothesis): bounds (i) and (ii) hold on every (cell, pool) with kappa_all of that pool. Any violation means the derivation or the code is wrong.
  • H11 (the residual, not the raw error, predicts screening cost): over the 11 cells, Spearman(kappa_q on the 128, median R over pools) >= 0.7 and exceeds Spearman(raw median |s - f|, median R) by at least 0.2. Refuted if Spearman(kappa_q, median R) < 0.5.
  • H12 (SPM against SPMe): on the 121 designs both completed, SPM@100's kappa_all is at most half SPMe@100's. Refuted if SPM's is not smaller.
  • H13 (mechanism): the least-squares affine residual of SPMe@100 against DFN@100 (121 designs) is correlated with SPMe's whole-run r_min more strongly than SPM@100's residual is: |Spearman| for SPMe exceeds SPM's by at least 0.2. Refuted if SPM's is at least as large. Not blind: milestone 2 already found r_min flags SPMe's large gaps (AUC 0.994); the SPM side and the residual form are new.
  • H14 (crossover): the corollary with p from kappa_q on the 128 and m = GP-EI's median DFN@100 calls on pools of 64 (9) predicts whether each of the four screens in milestone 4's pool sweep (SPM@2, SPM@100, DFN@2, DFN@10) has lower median T1 than GP-EI at pool sizes 16, 32, 64, 96. Supported if at least 13 of 16 calls are right, refuted if 10 or fewer. Not blind: the sweep's medians are in milestone 4's outcome; the formula has no fitted parameter, but the bound is conservative and may call losses that are wins.
  • Script: experiments/theory/run.py; outcome logged above this entry.

2026-11-11 · Milestone 4 outcome (search replay): a whole-pool DFN@10 screen is slower than plain GP-EI; the cheapest screens win on small pools, and GP-EI catches up by 96 designs

  • Replay of 12 methods on 30 pools of 64 of the 128 Sobol designs, each evaluation charged its median baseline fresh-run cost (experiments/search/results.txt). T1 = charged seconds until a design within 1% of the pool's best DFN@100 has been run at DFN@100.
  • H7 refuted: DFN@10 screen-then-verify has median T1 253.3 s against 220.4 s for GP-EI on DFN@100 (ratio 1.15, pre-registered bar 1/3), and at a budget of 73.5 s (GP-EI/3) it has not finished screening (regret 100%). Its first verified design is always within 1% (one DFN@100 call), but screening 64 designs at 3.6 s costs 229 s, more than GP-EI's median 9 DFN@100 calls.
  • H8 refuted by its letter, not in substance: successive halving over DFN cycles reaches 1% at 246.8 s against 253.3 s, lower on every pool (Wilcoxon p = 1e-7), a 2.6% saving. Charging resumed runs only the extra cycles brings halving to 184.8 s.
  • H9 supported: the SPM@2 screen (0.33 s a design) has median T1 168.2 s against 253.3 s for DFN@10 (p = 0.0003), and beats GP-EI (p = 0.01). Fastest overall: SPM@100 screen 153.2 s (95% 141.0 to 165.5) and DFN@2 screen 159.6 s, about 30% under GP-EI.
  • H10 supported: the trust flag speeds SPMe screening, 417.8 s against 699.5 s (p = 8e-5), because the DFN-best designs are among those SPMe flags. SPMe stays the slowest screen, slower than random DFN at the median (612 s).
  • MF-GP-EI (screen score as a fifth GP input) adds nothing on this pool: with DFN@10 it equals the screen (its start is already within 1%), with SPM@2 it is slower than the plain SPM@2 screen (192.7 against 168.2 s), because EI leaves the screen's order.
  • Not in the plan, pool-size sweep (30 seeds each): median T1 for GP-EI / SPM@2 / SPM@100 / DFN@2 / DFN@10 screens is 147 / 54 / 66 / 46 / 82 s at 16 designs, 220 / 168 / 153 / 160 / 253 s at 64 and 220 / 240 / 199 / 252 / 368 s at 96. Screening cost grows with the pool and GP-EI's barely does, so whole-pool screening is the right tool only for small candidate sets; a continuous search needs a model on the cheap rung, which is what the BOCA-style baseline (not run yet) should test.
  • Caveats: pools are drawn from one set of 128, so seeds share designs and the Wilcoxon p-values overstate independence; costs are one design's timings, so the screens' constant per-design cost hides that thick designs run up to 67 s under DFN.
  • Output: experiments/search/results.txt, summary.json, search.svg.

2026-11-11 · Milestone 4: which multi-fidelity search finds the DFN-best design for the least wall time? (plan, written before the run; H7 to H10 are this entry's)

  • Question: milestones 2 and 2a ranked single screens; a design loop also pays to screen. On the cached benchmark (experiments/cycles/bench.jsonl, no new PyBaMM runs), which search reaches a design within 1% of the best 100-cycle DFN score for the least simulated wall time: plain GP-EI on DFN, a screen with a cheap (model, cycles) cell then DFN verification in screen order, successive halving over DFN cycle counts, or GP-EI on DFN using a cheap screen as an extra input?
  • Replay: 30 seeds; seed s draws a pool of 64 of the 128 Sobol designs (random.Random(s).sample), so methods are compared paired on the same pools. Each evaluation is charged the median baseline wall time of a fresh run of that (model, cycles) cell from experiments/cycles/cost.json (e.g. DFN@100 24.5 s, DFN@10 3.6 s, SPM@2 0.3 s); a design counts as found only once run at DFN@100. Target: within 1% of the pool's best DFN@100. Primary metric T1: charged seconds until the best DFN@100 seen is within 1%. Every method continues until the whole pool is DFN@100-verified, so T1 is finite.
  • Methods: (a) random order at DFN@100; (b) GP-EI at DFN@100 (5 random starts, isotropic RBF on the 4 inputs scaled to [0, 1], length scale chosen from a grid by marginal likelihood, standardised y); (c) screen-then-verify for SPM@2, SPM@100, SPMe@100, DFN@2, DFN@10 (screen the whole pool, then DFN@100 in descending screen score); (d) SPMe@100 plus milestone 1's flag: the top 5 by SPMe, then every design with whole-run r_min <= 0.1 in SPMe order, then the rest; (e) successive halving over DFN at 2, 10, 30, 100 cycles with eta = 3 from the whole pool (Hyperband's most exploratory bracket), every rung charged a fresh run, then the remaining designs verified in order of their last rung's score; an incremental-cost variant (a resumed run pays only the extra cycles) is reported beside it; (f) GP-EI at DFN@100 with the DFN@10 or SPM@2 screen score as a fifth input (input-augmented multi-fidelity GP, after Kennedy and O'Hagan's autoregressive idea), the screen's top design as the start.
  • H7 (proposal H3, in wall time): DFN@10 screen-then-verify reaches T1 at median at most a third of GP-EI on DFN's median T1. Refuted if its median regret at a budget of a third of GP-EI's median T1 exceeds 2%.
  • H8: successive halving over DFN cycles does not beat the DFN@10 screen. Refuted if its T1 is lower in a paired Wilcoxon test at p < 0.05.
  • H9: the cheapest screen, SPM@2 (0.3 s a design), has a lower median T1 than the DFN@10 screen. Refuted if higher at p < 0.05 (paired Wilcoxon).
  • H10: the trust flag does not slow SPMe screening: SPMe@100 with the flag has median T1 no higher than SPMe@100 alone. Refuted if higher at p < 0.05.
  • Also reported: median and 95% bootstrap interval of T1 per method, median regret at budgets of 60, 120, 240 and 480 s, the number of DFN@100 calls to T1, and the paired Wilcoxon p for every method against GP-EI on DFN.
  • Limits fixed now: a pool replay, not a continuous search; costs from one design's timings; BOCA (continuous-fidelity BO) is not run in this step.
  • Script: experiments/search/run.py; outcome logged above this entry.

2026-11-11 · Milestone 2 outcome (dense benchmark): on 128 unbiased designs 10-cycle DFN beats 100-cycle SPMe at the same cost, and SPM beats SPMe

  • Context: this ran in parallel with milestone 2a (#14800, below), neither run seeing the other; 2a asked the same question on the 49 stratified designs, this asks it on a fresh 128-design Sobol sample, so it is the out-of-sample replication 2a's plan change called for. Both agree: DFN@10 against SPMe@100 is 0.977 against 0.834 on the 49 and 0.962 against 0.641 on the 128.
  • Benchmark: 128 Sobol designs x SPM, SPMe, DFN at 100 cycles, 384 runs, all committed per cycle (experiments/cycles/bench.jsonl). DFN completed all 128; SPMe failed on 7 (5%); SPM on none. Prefix check exact (relative difference 0 for all three models) and the baseline reproduces energy-cell-dfn exactly (SPMe 109.14, DFN 116.26 Wh/kg).
  • H1 supported: Spearman with DFN@100 is 0.962 for DFN@10 against 0.641 for SPMe@100, a difference of +0.32 (paired bootstrap 95% +0.18 to +0.48).
  • H2 supported, narrowly: DFN@10 takes 3.6 s and SPMe@100 3.7 s on the baseline (median of 3, idle machine), ratio 0.98.
  • H3 supported: DFN@10 screen plus top-10 DFN@100 verify finds the DFN best of the 128 (162.3 Wh/kg, regret 0%; in fact from k = 1). The SPMe@100 screen misses it at every k up to 20 (regret 1.98%) because SPMe ranks the DFN-best design 41st, scoring it 121.0 (gap 0.25).
  • Not in the plan, and the finding to follow up: the plain SPM, which has no electrolyte at all, ranks better than SPMe (Spearman 0.955 at 100 cycles), and still does over the 121 designs SPMe completed (0.984 against 0.769), so SPMe's problem is not only its solver failures. SPM over-scores by a median +7.1 Wh/kg and SPMe under-scores by -8.7, but SPM's error is closer to a uniform shift. SPM is not a safe screen for the single best design (top-1 regret 9.4%, it scores the DFN best at 182.7), only for a shortlist (regret 0 from k = 5).
  • Also not in the plan: on this unbiased sample milestone 1's label marks 15 of 128 designs (12%) untrusted under SPMe, against 7 of 49 in the stratified sample; SPMe's minimum salt concentration over the 100-cycle run flags them with AUC 0.994, and r_min <= 0.1 catches all 15 with 8 false flags. (Milestone 1's flag used a 2-cycle run; this one is the whole run's minimum, so it is a replication of the signal, not of the exact test.)
  • SPMe's agreement falls with cycle count (0.736 at 2 cycles, 0.641 at 100): its error grows as degradation accumulates, while DFN's short runs converge to the 100-cycle ranking (0.942, 0.962, 0.980 at 2, 10, 30).
  • Plan change (agrees with 2a's): the milestone 4 search uses (model, cycles) as a two-axis fidelity space with DFN at short horizons and SPM as the cheapest rung; SPMe stays only as the source of the trust flag. Milestone 3's theory should explain why the SPMe correction hurts design ranking when it is meant to help voltage.
  • Output: experiments/cycles/results.txt, summary.json, cost.json, prefix.json, bench.jsonl, cycles.svg.

2026-11-11 · Milestone 2 (dense benchmark): is the cycle count a better fidelity axis than the model? (plan, written before the run; numbered H1 to H3 within this entry)

  • Question: milestone 1 found the cost is in the cycle count (100-cycle DFN 27.9 s, 2-cycle DFN 1.3 s), not in the model. Does a short DFN run rank designs by their 100-cycle DFN score as well as a full 100-cycle SPMe run does, at lower cost? The answer decides which axis the multi-fidelity search of milestone 4 spends its budget on.
  • Data: a new paired benchmark, 128 designs from a scrambled Sobol sequence over the energy-cell bounds (scipy.stats.qmc.Sobol, d = 4, seed 0, random_base2(7)), not chosen by any search, so it is not the stratified sample of milestone 1. Each design runs once per model (SPM, SPMe, DFN) for 100 cycles of the energy-cell protocol (OKane2022, 5 A discharge to 2.5 V, 5 A charge to 4.2 V, SEI and plating on), one fresh process per run. Each run stores the discharge energy of every cycle, so the score at cycle n (Wh/kg of cycle n, energy_cell.cell.evaluate's rule: 0 when the run stops before cycle n) comes from the same run for n = 2, 10, 30, 100. Prefix validity (an n-cycle run equals the first n cycles of a 100-cycle run) is checked on the baseline before use. The baseline's 100-cycle SPMe and DFN scores must reproduce energy-cell-dfn's 109.14 and 116.26 Wh/kg within 0.5%.
  • Cost: wall time of an n-cycle run on the baseline for each model and n, fresh process, median of 3, on an otherwise idle machine (the benchmark runs three at a time, so its own timings are not used for cost).
  • Target: DFN at cycle 100 (DFN@100). Designs DFN fails on (score 0) stay in, as ties at the bottom.
  • H1: Spearman(DFN@10, DFN@100) is at least Spearman(SPMe@100, DFN@100). Refuted if it is lower by more than 0.05.
  • H2 (cost): a 10-cycle DFN run costs no more than a 100-cycle SPMe run on the baseline. Refuted if it costs more than 1.5 times as much.
  • H3 (screen then verify): screening all 128 with DFN@10 and DFN-verifying the top 10 at 100 cycles finds a design within 1% of the DFN@100 best of the 128; refuted if the regret exceeds 2%. The same for SPMe@100 as the screen is reported beside it.
  • Also reported (no hypothesis): the full grid (SPM, SPMe, DFN) x (2, 10, 30, 100 cycles) of Spearman and top-10 overlap against DFN@100 with bootstrap intervals, and each cell's cost, so the cheapest cell that ranks as well as SPMe@100 can be read off.
  • Script: experiments/cycles/run.py; outcome logged above this entry.

2026-11-11 · Outcome 2a: a 10-cycle DFN run ranks 100-cycle DFN far better than a 100-cycle SPMe run, at the same wall time

  • H4 supported: Spearman(DFN at cycle 10, DFN at cycle 100) = 0.977 against 0.834 for 100-cycle SPMe; paired bootstrap of the difference over designs 0.138 (95% 0.057 to 0.271). DFN at cycle 30 reaches 0.990, and even DFN at cycle 2 (0.915) beats every SPM and SPMe rung (best: SPMe at cycle 10, 0.883).
  • H5 at the boundary, read as equal cost, not cheaper: median DFN wall time to the end of cycle 10 is 4.0 s against 4.1 s for a whole SPMe 100-cycle run (ratio 0.98, supported by the plan's measure); cycle-end to cycle-end it is 4.0 against 3.7 s (1.07). Not refuted (threshold 1.5).
  • H6 supported: DFN-verifying the top 5 by DFN at cycle 10 finds the DFN best of the 49 (regret 0) where the top 5 by SPMe 100 misses by 2.1 Wh/kg. At k = 1 DFN at cycle 10 picks a design 2.5 Wh/kg short (SPMe 100: 2.1).
  • The reduced models get worse with horizon: SPMe's Spearman peaks at cycle 10 (0.883) and falls to 0.834 at 100, so its degradation path drifts from DFN's. DFN keeps only 58 to 74% (median 61%) of its cycle-10 energy by cycle 100, so the short run ranks well despite heavy fade, not because nothing fades.
  • The 7 milestone-1 untrusted designs: mean absolute rank error 4.6 places under DFN at cycle 10 against 16.3 under SPMe 100; the three SPMe solver failures solve under DFN.
  • Negative: a linear fade extrapolation of DFN from cycles 2 and 10 to cycle 100 ranks at Spearman 0.01 (early fade is not linear); rank on the raw cycle-10 score instead.
  • Reproduction: the SPMe 100-cycle re-runs match the committed spme_now scores exactly (max difference 0) and a DFN 100-cycle re-run of design 0 matches its committed 116.256 Wh/kg.
  • Plan change for milestone 2 (dense Sobol benchmark): cache DFN per cycle up to 100 (one run gives every rung) plus SPMe 100, and run the search comparison with cycle count as the fidelity axis; the trust flag from milestone 1 stays as a check for searches that do use SPMe.
  • Output: experiments/horizon/results.txt, horizon.jsonl, summary.json, check.json, horizon.svg.

2026-11-11 · Milestone 2a: is a short DFN run a better screen than a full SPMe run? (plan, written before the run)

  • Question: milestone 1 found that cycle count, not model reduction, carries most of the cost (DFN 100 cycles 27.9 s against 1.3 s for 2 cycles on the baseline). If the ranking of designs by DFN at cycle 10 already matches the 100-cycle DFN ranking, a short-horizon DFN screen beats the full-horizon SPMe screen the multi-fidelity literature would reach for. This is the fidelity grid the outcome entry below asked for (model x cycles), run before the dense Sobol benchmark (proposal milestone 2) so that benchmark caches the right rungs.
  • Data: the same 49 designs, the same protocol and OKane2022 parameters, PyBaMM 26.10.1.1 (as committed). New runs, one process per design and model: SPM 100 cycles, SPMe 100 cycles, DFN 30 cycles, recording the discharge energy of every cycle and the wall time at the end of every cycle (PyBaMM on_cycle_end callback, set-up included). Score at cycle n = discharge Wh of cycle n / stack mass, the energy-cell score with cycles = n; 0 if the run did not complete n cycles. Reference: the committed 100-cycle DFN scores (energy-cell-dfn/experiments/dfn.jsonl); a check re-runs DFN 100 cycles on design 0 against its committed 116.26 Wh/kg.
  • Comparator: 100-cycle SPMe against 100-cycle DFN, Spearman 0.834 on the committed scores (computed before this plan; it is the milestone 1 data).
  • H4 (ranking): Spearman(DFN at cycle 10, DFN at cycle 100) is at least 0.90. Refuted if below 0.834 (no better than full SPMe).
  • H5 (cost): the median over the 49 of DFN wall time to the end of cycle 10 is at most the median SPMe 100-cycle wall time. Refuted if above 1.5 times it.
  • H6 (screen): DFN-verifying the top 5 by DFN cycle 10 has regret to the DFN best of the 49 no larger than the top 5 by SPMe 100 (2.1 Wh/kg). Refuted if larger.
  • Also reported (no hypothesis): Spearman and top-k regret for every rung (SPM, SPMe at 2, 10, 30, 100; DFN at 2, 10, 30), a linear extrapolation of DFN to cycle 100 from cycles 2 and 10, and where the 7 milestone-1 untrusted designs rank under DFN at cycle 10.
  • Script: experiments/horizon/run.py; outcome logged above this entry.

2026-11-11 · Outcome: the flag works (AUC 0.997), but cycle count, not model reduction, is where the cost is

  • H1 supported: SPMe's 2-cycle minimum electrolyte concentration (r_min) separates the 7 untrusted designs from the 42 trusted with ROC AUC 0.997 (bootstrap 95% 0.980 to 1.000). The 3 solver failures count as r_min = 0 by the plan; over the 46 designs SPMe solved, AUC is 0.994 (4 untrusted). A flag at r_min <= 0.10 catches all 7 with 1 false flag (design 30, gap 0.17); at r_min <= 0 it catches 6 with none.
  • H2 supported: Spearman(r_min, relative gap) = -0.833 over 49.
  • H3 refuted, and this is the finding that changes the plan: a 2-cycle run costs SPM 0.3 s, SPMe 1.2 s, DFN 1.3 s (median of 3, baseline design, fresh process, set-up included), so SPMe/DFN = 0.88. Extra run, not in the plan: at 100 cycles, SPM 1.0 s, SPMe 3.9 s, DFN 27.9 s (one run each), SPMe/DFN = 0.14. Going from 100 cycles to 2 saves 21x on DFN; going from DFN to SPMe at 100 cycles saves 7x. A 2-cycle DFN run costs no more than the 2-cycle SPMe flag, so the cheapest trustworthy screen may be short-horizon DFN, not SPMe.
  • Replay: DFN-verifying the top 10 by SPMe already returns the DFN best of the 49 (163.0); the top 1 to 5 returns 160.9 (regret 2.1, 1.3%). Adding the flagged designs costs 8 DFN calls and finds nothing better, because the designs SPMe mis-scores are not the DFN optimum in this sample. The flag's value is in not pruning a region, not in the best design here.
  • Plan change: milestone 2 adds the cycle count as a fidelity axis (2, 10, 30, 100 cycles x SPM, SPMe, DFN) and asks whether early-cycle DFN ranks 100-cycle DFN as well as 100-cycle SPMe does.
  • Output: experiments/trust/results.txt, probe.jsonl, cost.json, cost100.json, summary.json, trust.svg.

2026-11-11 · Milestone 1: can the cheap model flag where it cannot be trusted? (plan, written before the run)

  • Question: energy-cell-dfn found that SPMe and DFN agree on most of 49 energy-cell designs (median gap 9%) but disagree badly on a few (SPMe 0 to 27.6 Wh/kg where DFN gives 120 to 146), and traced the failures to electrolyte salt depletion. A multi-fidelity search needs to know before paying for DFN which cheap scores to distrust. The candidate indicator is free: SPMe's own minimum electrolyte concentration, read from a short SPMe run.
  • Data: the 49 designs of energy-cell-dfn/experiments/selected.json with their committed 100-cycle SPMe and DFN scores (dfn.jsonl, not re-run). New runs: each design under SPMe for 2 cycles (5 A discharge to 2.5 V, 5 A charge to 4.2 V; the energy-cell protocol and OKane2022 parameters), recording the minimum electrolyte concentration over space and time divided by the initial 1000 mol/m3 (r_min), whether the solve failed, and wall time. A solver failure counts as r_min = 0.
  • Label (fixed now): a design is untrusted when SPMe's cycle-100 score is below DFN's by more than 25% of DFN's ((DFN - SPMe) / DFN > 0.25), or SPMe scored 0.
  • H1: r_min separates untrusted from trusted designs with ROC AUC at least 0.90. Refuted if AUC < 0.80.
  • H2: across all 49, r_min and the relative gap (DFN - SPMe) / DFN have Spearman correlation at most -0.5. Refuted if above -0.3.
  • H3 (cost): one 2-cycle SPMe run costs under a tenth of a 2-cycle DFN run on the baseline design (wall time, 3 repeats each, one process). Refuted if the ratio is above 0.25.
  • Also reported (no hypothesis): the screen-then-verify replay on the committed scores (DFN on the top-k by SPMe, with and without the flagged designs added), and its regret to the DFN best of the 49.
  • Script: experiments/trust/run.py; outcome logged above this entry.

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Produced with AI assistance (Claude). Results are from the code in this repository and are simulated or stylised unless the abstract says otherwise; nothing here implies affiliation with or endorsement by any lab, researcher or company cited. MIT licensed.