1059 projects across 31 themes, from proper scoring rules and verifiable decentralised ML training to digital twins, chip-design loops and robot manufacturing. Each project states a question, answers it with its own code and tests, and lists its limitations. The incentive work builds on algorithmic economics and information elicitation (CU Boulder, Frongillo, Waggoner) and Gensyn's verifiable-ML work.
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Peer-prediction and prediction-market mechanisms for verifying decentralized ML training, with adversarial evaluation.
Read more → Markets as routersCost-function markets as expert routers: LMSR = Hedge, quadratic potential = sparsemax; regret/loss bounds verified, continual-learning simulation.
Read more → Verification games & slashingInspection-game economics of refereed verification: stake substitutes for re-execution, extra verifiers free-ride, and optimal tolerance/stake under floating-point drift.
Read more →Research logs
Latest: 2026-10-20 · Flexible models and a pooled nine-survey model: neither beats the single-lens additive models where data are large
Read the log → Ongoing · verifiable-training-mechanismsLatest: 2026-10-31 · Milestone 53: does a progress check (loss on a verifier-held batch every N steps) close the liveness hole that norm checks leave? (H4/H3 link, planned before running)
Read the log → Ongoing · lowcomm-trainingLatest: 2026-10-31 · Milestone 6n (H6 scale-up): is the size-2 excess linear in omega? Keep 1/4 at H = 64, six seeds (planned before running)
Read the log → Ongoing · aerolog-scalingLatest: 2026-10-31 · Milestone 9o: can the output-error fit estimate the noise correlation itself and still recover 9n's gain? (planned before running)
Read the log → Ongoing · sim2real-inferenceLatest: 2026-10-30 · Milestone 7y: finite-pool certificate moves into the main text (a writing step, no experiment)
Read the log → Ongoing · verified-dseLatest: 2026-10-31 · Milestone 45: does the rank displacement rho/k grow with pool size? (exploratory; no predictions were written before the script ran)
Read the log → Ongoing · heavy-hydraulicsLatest: 2026-10-31 · Milestone 3j: the manual's P-to-A flow curves pin the rating-point drop (not pre-registered)
Read the log → Ongoing · marine-hullLatest: 2026-10-31 · Milestone 7e: H5 for the glider against the propeller AUV: what fixed-energy gap flips the order? (not pre-registered)
Read the log → Ongoing · marine-pathLatest: 2026-10-30 · Milestone 1: LOS against integral LOS (hypotheses written before the sweep)
Read the log → Ongoing · swe-orgsLatest: 2026-10-21 · Batch 22: reminding the owner of a pull request that has gone overdue
Read the log → Ongoing · capture-trackpriorLatest: 2026-10-29 · Gated tracking with re-acquisition (planned, then results below)
Read the log → Ongoing · llm-coding-inferenceLatest: 2026-10-31 · Milestone 7e: the 2,000-draw check moves into the paper and README (a writing step, no experiment)
Read the log → Ongoing · build-dataLatest: Session 7, 2026-10-31: milestone 4 instrument (split-conformal, drift diagnostic); not run on real data
Read the log → Ongoing · civ-leversLatest: 2026-10-31 · Lagged elite recruitment and lagged stress (milestone 7, second run)
Read the log →What should a verifier be paid for its report? Proper scores for probabilities, intervals, quantiles, rankings and vectors, and the regret each one leaves. Topic page →
Property elicitation (quantile/expectile/Bregman scores, non-elicitability of variance) applied to pricing tail-drift tolerance thresholds in verifiable ML training.
Finite-precision probability reports under proper scoring: optimal-grid regret law matched to 0.3%, uniform grids lose a ln N factor under log score, raw minifloat formats are ~13× worse than symmetrised.
Risk-averse verifiers under proper scoring: log score reports exactly odds^(1/(1+αb)), Brier reports solve logit p = logit r + k(2r−1) and can be debiased exactly, a mean-k aggregation correction is worse than none, and a binarised lottery rule is truthful for any utility at a 2.6–27% certainty-equivalent cost.
Selective reporting under proper scoring: abstention iff |p−α| < √c (Brier), silence is evidence unless the anchor is a symmetric prior, ignoring it costs 30× the log-loss at n=12, and a stale anchor makes silence point at the wrong state.
Jointly eliciting VaR and expected shortfall of benign drift with a scale-free Rockafellar–Uryasev score: ES alone is not elicitable, misreport cost is exactly ln r + 1/r − 1, quantile-only tolerances leave a/(a−1) of the Pareto tail uncovered, and auditing tail reports breaks down at index ≤ 2.
Paying verifiers for resolution, not calibration: raw Brier/log excess is exactly E[(r-p)²]/E[KL(p‖r)], Brier is bounded but log is not, log-score selection reverses for overconfident high-resolution verifiers (a ≥ 2.49), and n-sample recalibration costs tr(HI⁻¹)/2n (0.264/n).
CRPS vs log score for continuous drift reports: exact Gaussian closed forms, overconfidence capped at 0.234σ under CRPS (unbounded under log), 1-Lipschitz outcome sensitivity, plug-in cost 5σ/(8√π n), and finite score variance for tails ν>2 vs ν>4.
Eliciting drift variance from two independent re-executions: D=(y1−y2)²/2 unbiased with Var=σ⁴(κ+1)/2, exact Brier and scale-free misreport costs (1/λ+ln λ−1), detection needs ≈2z²(κ+1)/(λ−1)² tasks, disjoint pairs 1.8× worse than the sample variance, heavy tails break m^{−1/2} concentration.
Eliciting drift *variance* from pairs of independent draws: exact pair score (excess loss (r−σ²)²), degree table (mean² 2, third moment 3, σ⁴ 4), audit cost ((z_α+z_β)/ρ)²(κ+1)/2 pairs, robust Gini score beats it for heavy tails, all-pairs pooling saves (κ+1)/(κ−1), correlated draws bias the target to σ²(1−ρ).
Bounded-payment log score by quadratic tangent extension: strictly proper, log-identical on [ε,1−ε], worst-case payment exactly ln((1−ε)/ε)+1/(1−ε), 63× Brier's curvature per range at p=10⁻³, crossover p(1−p)=1/(2R), best cutoff ε=p.
K-ary proper scores: exact worst-case regrets (1−2p_min+‖p‖² Brier, ‖p‖−p_min spherical), spherical beats Brier by exactly √K per payment range at a uniform truth, and both bounded scores nearly ignore a dropped rare class (1e-4 vs 0.15 for log).
Bounded multiclass log score by quadratic tangent extension of x ln x: log-identical when all r_j≥ε, payment range exactly 1−ln ε for any K, 63× Brier's rare-class incentive per range at ρ=10⁻³ with best cutoff ε=p_min, and a closed-form bounded cost for dropping a rare class.
Eliciting class rankings with linear rank-weight scores: strictly proper, adjacent-swap regret exactly (p_i−p_j)(w_r−w_{r+1}), beats Brier-derived rankings per unit range below gap 1/(K−1) (250× at gap 10⁻³), equal spacing is optimal, top-k set costs the same as the mode, detection sample size unchanged.
Ranked probability score for ordered severities: exact regret Σ(R_k−P_k)², shift over distance d costs dε² (Brier 2ε²), pooling adjacent classes costs half of Brier's, threshold errors ≤ √regret, and per range RPS never beats Brier's incentive.
Jointly eliciting VaR and expected shortfall of benign drift: 0-homogeneous Fissler–Ziegel score minimised at (VaR, ES) with profile ln ES, ES alone non-elicitable (mixture 12.5 vs 10), exact regret formulas, ES-understatement of 30% detectable with ~1k samples at τ=0.95 while pinball is blind.
Eliciting the modal drift with the window loss 1[|y−r|>α]: exact window-mass regret, best width α=σ (normal) / γ/√3 (Cauchy), closed-form critical width α* above which bimodal drift has one α-mode, and 0 bias against contamination where the mean moves 5ε.
Companion to interval-elicitation: Winkler interval score for drift-tolerance intervals: strictly proper for the α/2 and 1−α/2 quantiles, closed-form regret, optimal expected score 4sφ(z)/α, width-misreport costs whose asymmetry flips with the level, and Cauchy drift where scores have no mean but paired differences are bounded.
Paying for a drift tolerance interval: Winkler interval score is proper for the equal-tailed pair with exact regret (finite for Cauchy) but unbounded payment; the bounded width-plus-miss loss elicits the shortest interval (22–31% narrower on lognormal drift) at a 3–48× larger detection sample for α≥0.1.
Scoring a verifier's vector report: the precision score Σ⁻¹ is uniformly most detectable among quadratic Bregman scores (Cauchy–Schwarz), an isotropic score can need (1+κ)²/(4κ) times more tasks (25× at κ=100, power 0.29 vs 0.80), diagonal normalisation barely helps, estimated precision reaches 0.61 efficiency at m=2d draws.
From a verifier's excess proper score to a certified cap on accept/audit/slash decision regret: exact calibration functions (Brier ε², log KL), linear transfer only for non-proper hinge, audit action tightens the guarantee.
Polyhedral surrogates for accept/reject/escalate verifiers: minimiser embeds the Bayes action, linear regret transfer with constant exactly 2d, logistic transfer ratio 2d(1-d)/δ, and a negative SGD result.
Scoring verifiers whose report decides acceptance and whose outcome is seen only on acceptance: a truthful reserve exists iff the score centre τ_s ≥ τ_d (unique c0 = 1+τ_d²−2τ_dτ_s), plain Brier fails above τ_d = ½, recentring fixes it at rent τ³/3, exploration costs 1/ε payment variance.
Scoring verifiers against a noisy judge: raw proper scores elicit e0+γp and shrink Brier incentives by γ², can reverse rankings (η*=0.25), the unbiased surrogate score is exactly proper at a 1/γ payment spread and 1/γ² sample cost, and misestimated rates give a closed-form bias.
Scoring when truth exists only on audited tasks: report-dependent audit rates make naive scoring improper (shift −bp(1−p)/(2(a+bp)), full hiding for steep rates), inverse-propensity weighting is exactly proper for any audit rule, and Neyman allocation gains only 3–11% variance.
Calibration tests are gameable: an information-free Foster–Vohra/Blackwell hedger keeps expected ECE ≤ √(K+1)(1/(2K)+1/√T) against any outcome sequence (measured 0.016, Brier 0.254 vs 0 informed), so slashing must use a resolution-sensitive score; a Brier-gap test detects it in 100/100 runs.
Eliciting the chance two honest runs of a nondeterministic op agree (Γ=Σp²) from run pairs: proper with exact regret, one run provably cannot, all-pairs U-statistic variance ~¼ of disjoint pairs, fleet of H hardware classes false-slashes strict equality at 1−H^{1−k}, colluders' blind spot at ε=2Γ/(1+Γ).
Brier skill scores normalised by the realised base rate are improper: exact optimal report, ≈ −(1−2p)/n bias, cross-task leakage through the pooled baseline, and a leave-one-out fix.
Original U.S. marriage microdata: interpretable annual-divorce models, schooling/earnings pairings and reproducible held-out validation; no validated personal optimum.
Paying for costly checking when effort is hidden and ground truth may never arrive. Topic page →
Peer-prediction and prediction-market mechanisms for verifying decentralized ML training, with adversarial evaluation.
Paying verifiers for costly checking effort with proper scoring rules: implementable efforts = concave envelope of the value curve, exact Brier rent (n−1)/(a+b), log score needs half Brier's payout spread on rare-fault priors.
Scoring rules as limited-liability effort contracts: shirking threshold 2c/(kκ²), first best needs a fee, otherwise the principal keeps 48–68% of surplus.
Peer prediction without ground truth: output agreement pays 1.0 for laziness vs 0.68 for honesty, Dasgupta–Ghosh payoff 2p(1-p)g_i g_j exact, effort as a coordination game with threshold c/(2p(1-p)κ²), and closed-form gold-check rate √(c·g_H/G).
Peer prediction when lazy verifiers share a default answer: agreement pay is 2G·Cov, effort is a coordination game with threshold a*=(k/2G+s)/(pq+s), the all-lazy equilibrium always exists and pays as much as honesty when the default matches the prior, and gold checks needing more mass than the honest pay close it.
Finite-sample noise in multi-task peer prediction: the plug-in payment is 2× the sample covariance with an exact variance (matches enumeration), √2 less noisy than fresh penalty tasks, pays a constant reporter 0, and a lazy coin still earns ≈σ/√(2π) under limited liability; deductibles and detection/ranking sample sizes in closed form.
Surprisingly-popular verdicts for rare-but-diagnostic signals: majority errs 0.84 on faulty jobs at n=101 when detection is 0.45, SP is an exact fraction threshold v/(1−u+v) (2.1×10⁻⁵ error, 47 votes for 10⁻³ vs Bayes 36), a wrong believed prior wrecks finite-n accuracy, a wrong believed detector breaks the limit, Byzantine breakdown at exactly 13.6%.
Sequential verifiers who see earlier verdicts herd: wrong-cascade probability exactly (1−a)²/(a²+(1−a)²), cascade after 2/(a²+(1−a)²) signals, accuracy capped at 0.845 (a=0.7) versus ≈1 for an independent majority, and a sealed first batch of ≥3 lifts the cap (0.875 at m=3, 0.949 at m=11); checked against Bayesian agents.
Verifiers who choose when to stop checking under a proper score: optimal policy is a symmetric threshold (matches dynamic programming), closed-form accuracy 1/(1+((1−a)/a)^k) and cost k(2p_k−1)/(2a−1), participation κ ≥ 4c/(2a−1)², and adaptive stopping matches fixed-sample accuracy with 2–3× fewer checks.
Stake, audits, bribes and disputes: the equilibrium economics of refereed and optimistic verification. Topic page →
Inspection-game economics of refereed verification: stake substitutes for re-execution, extra verifiers free-ride, and optimal tolerance/stake under floating-point drift.
Bribing verifiers in refereed verification: closed-form bribe floor, a sharp collusion-proof stake that falls as 1/m, and jackpots that raise the floor one-for-one.
No-regret learning in the refereed-verification inspection game: conserved potential, closed-form cycle period, averages converge but per-round audit probability collapses; optimistic Hedge converges.
M verifiers in the inspection game: detection pinned at s/(s+S), cheating rises with m under split rewards, symmetric equilibrium is a saddle (volunteer's dilemma), bandit learners need an exploration floor.
Sampled audits of committed training traces: payoff is convex in corrupted steps, deterrence iff min(F, f·k) ≥ T·g, so stake and audits are complements and stake must scale with job length.
Random k-fold replication with slashing against a colluding fraction β: secret assignment makes cheating a coordination game with unique-honesty stake Gβ^{k−1}/(1−β^{k−1}), public assignment leaves β^k corruption at any stake, and assignment leaks leave a λβ^k floor.
Scarce audit budget across heterogeneous jobs: deterrence threshold g/(g+S) makes it a knapsack, greedy with a 1/3 guarantee (within 1% on 91% of instances), uniform audits need up to 1.9× the budget, heterogeneity lowers deterrence cost (Jensen), stake substitutes for audits.
Staffing the audit pool that stake-based deterrence needs: exact Erlang-C waiting (matches simulation), square-root staffing R+1.06√R (spare capacity 60% at R=5, 1.1% at 10⁴), stake–headcount optimum G+S=√(wsG/(rd₀)) (cost 24 vs 77 at too little stake), and bursty audit demand delays 1.8× what Allen–Cunneen predicts.
Escalating-bond dispute games: exact deterrence opening bond εV/((1−ε)C−εD) shrinks geometrically in rounds while the attacker's total outlay barely moves, and a sharp capital race where the defender needs γ·max{C(r) ≤ B_C} ≤ γ·B_C.
K-ary bisection dispute games: optimal arity solves k ln k − k + 1 = a/b (binary only if a/b ≤ 0.386), 1.9–6× cheaper than binary at T=10⁶, adaptive schedules gain ≤1%, leaf-size trade-off, latency as extra round cost.
Optimistic-verification challenge windows with bribable proposers: exact gamble-then-bribe attacker recursion, closed-form window, stake cannot shorten it under an exogenous bribe price (63 blocks for S=10…1600), bounty-funded priority fees give S·w ≈ G/((1−ρ)θ).
Escalating jury appeal ladders with fee-priced appeals: an exact fee window makes error ∏(1−M_k), 11 jurors is the smallest deterring panel at prize 100, 3→11→27 errs 2.4e-4 at 5.8 expected seats vs 12.6% for one 7-seat panel, shared jury bias sets a floor ρ(1−a).
Hash-derived audit challenges under free retries: cheat profit exactly G − c/p, deterrence needs ln(G/c)·T/k opened steps vs ln2·T/k for a beacon (10×–60×), stake is irrelevant, and the proof-of-work optimum is x* = v/λ_p − c0.
Verifiers as informational complements: decision value is zero below a closed-form committee size while mutual information is submodular; myopic hiring buys nothing and leave-one-out pay is a sawtooth that vanishes.
Verifier committees from a finite pool: exact hypergeometric capture (zero once m ≥ 2B+1, up to 26× below binomial), exact size ≈0.90 of ln(1/ε)/KL(½‖β) vs Hoeffding up to 2.2× too large, stake-weighted draws depend only on Byzantine stake share (20 of 100 nodes at 4× stake capture a 41-committee w.p. ½), and the threshold safety/liveness trade-off.
Identity splitting vs merging under stake-weighted pools: split-invariant iff the weight is linear in stake, per-head optimum √(Rn/c)−n, sharp deterrence fee Rn/((n+1)(n+2)), wagering split-neutral.
Can a bond tell reliable hardware from unreliable? Single crossing runs the wrong way: reliable rent (θ_H−θ_L)(c+(1+ρ)s_H)/(1−θ_H) is minimised at zero stake, a flat wage is optimal, and a deterrence stake scales rent by (c+(1+ρ)s)/c.
Milestone payments without enforcement: a split pre-payment needs only the pooled relationship value (C/(W_r+W_w) vs P/W_r, C/W_w), and front-loading makes the milestone count logarithmic, ⌈ln(1+(V−C)/W)/ln(V/C)⌉ (17 vs 100 at W=1).
Research programme: incentive-compatible verification of outsourced ML training; first measurement on real training finds a tolerance-tau referee passes a skip-steps cheat on 30% of steps at tau = 1e-2 while the held-out loss stays within one seed std, and the loss only suffers at tau about 10x the worst benign drift; milestone 4 prices contracts by linear programme: with a tolerance, audit-only cannot enforce full effort and the joint contract beats both checks only when the score is precise (4 of 45 cells); milestone 6: against a coordinating majority replication adds no deterrence beyond the audit and the stake is flat in the number of workers (140 cells); milestone 5: an agreement term between redundant workers is worth nothing beyond the audit once cheats copy one trajectory (0 of 1,349 random instances), and a proved one-sided bound max(C, g/p - S) holds in 2,755 instances but is vacuous for a noisy score
Statistics for catching cheats under floating-point noise: tolerances, anytime-valid tests and robust aggregation. Topic page →
Measured float32 reduction-order drift, RepOps-style canonical order, Merkle-committed training traces with a teacher-forced referee; per-step tolerance is a cumulative hidden-deviation budget.
Calibrating slashing tolerances from honest runs: split-conformal false-slash law (n+1-k)/(n+1) is exact but only ~51–56% of calibration sets are ≤ α, PAC safety needs n ≥ ln δ/ln(1−α) (459 at 1%/1%), the margin is cheater hiding room (×1.26 at n=2000, Pareto-3), Gaussian plug-ins over-slash skewed drift up to 17×, pooled hardware calibration over-slashes the noisy class 4.8× and lets the quiet class hide 2.9×.
Per-layer vs total drift tolerances: a tolerance per layer admits L·c(L,α)σ vs z_α√L σ on the total (6.6× at L=16), the sum test ignores how a cheat is spread while the max test catches 2.7σ in one layer but lets 16σ through spread over all, and a union test caps the hidden budget at the sum test's.
Freivalds' matrix-product check in floating point: rank-one corruption missed with probability exactly erf(t/(√2F)) (worst case for fixed norm), erf^m for m probes, Rademacher probes stuck at ½ for any size, measured float32 noise floor, and 1/erf grinding tries when the probe is hashed from the result.
Detecting skipped training steps from the loss alone: hidden compute is the loss curve inverted at the noise band (f* = 1−(1+(e^q−1)/r)^{−1/β}), grows as reducible loss falls, seed noise sets a floor no eval size removes, simulation matches within 1.5 points, and the loss test is worth ≈4.4 step audits at best.
Detecting a provider that serves a cheaper model on a fraction of queries: mixture e-process (valid under peeking), delay ∝ 1/(f p² χ²), so the cheater's best response is to leak rarely and steal ∝ √N not N; closed-form audit rate and cost-optimal check rate (hK/2Nc)^{2/3}.
Anytime-valid slashing of miscalibrated verifiers: peeking z-test falsely slashes 37% of honest verifiers (nominal 5%), an e-process holds ≤α by Ville, detection delay ≈ ln(1/α)/KL (within 12%), q-free mixture costs ×1.36.
Anytime-valid duels between two verifiers: the optimal betting e-process on the Brier difference grows at exactly KL(q‖(rA+rB)/2), a peeking z-test falsely declares a winner 19–38% of the time at nominal 5%, a bet mixture stays ≤3.8% and costs 15–41% more decisions.
Anytime-valid best-of-n verifier identification: delay set by the rival whose report midpoint sits nearest q (the best opposite-side rival, not the runner-up), mixture within 1.35–1.60× of oracle, elimination 4–5× cheaper, peeking declares a false best in 59% of ties vs 1.6%.
Byzantine-robust aggregation of verifier reports: mean bias βB unbounded, median bias σΦ⁻¹(1/(2(1−β))) independent of B, trimmed-mean closed form for τ≥β verified by simulation.
Auditing skipped or partial continual-learning training from old-task losses: exact loss law (ρ^{t−1}[(1−2m₁+m₂)(r/d)λᵏ+(r/d)ρ(ρᵏ−λᵏ)]), a skipped task is ≥ d/(d−r)× worse but only clearly so inside a lag window, detecting a skipper takes ~0.7/s² jobs at any lag, a 10% step shortfall needs ~9600.
Interference-free or mean-noise-rise radar twin vs intermittent mutual radar interference between robots: exact closed-form per-frame Pd, real Pd plateaus at 0.656 (no-hit probability), mean-rise twin 9% optimistic at Pd ≥ 0.9 yet badly pessimistic for hit-tolerant missions, geometry knowledge helps 9-of-10 missions (Brier 0.089 vs 0.101). Stylised.
Net3 leak signals under demand-driven and pressure-driven demand (WNTR): identical at 1 to 1.25 times base demand and nearly so at 1.5 times; beyond that both models fail because the pumps cannot meet demand (simulated; one network).
Water-leak detection from pressure residuals on EPANET's Net3 (WNTR): at a 5% weekly false-alarm budget, 5 sensors and 10% demand error, CUSUM finds all leaks the sensors can see at 4% of demand but 8% at 1% (3% of all leaks); demand error, not sensor noise or detector choice, sets the limit (simulated leaks; BattLeDIM L-Town was unreachable).
Cost-function and wagering markets as online learners that route among modular, continually learning experts. Topic page →
Cost-function markets as expert routers: LMSR = Hedge, quadratic potential = sparsemax; regret/loss bounds verified, continual-learning simulation.
Self-financed wagering mechanisms as verifiable routers for modular, continually learning experts; shows plain WSWM locks in under recurring regimes and a fixed-share tax fixes it at the cost of subsidising free-riders.
Pooling calibrated experts with shared training data: Bayes-optimal extremization a* = n/(1+(n−1)ρ) verified numerically, saturation at n_eff → 1/ρ, asymmetric robustness, and online learning of the exponent.
Hedge/LMSR routing with delayed feedback: regret ≤ ln N/η + ηT/8 + ηD/2 (mean delay inflates horizon by 1+4d̄), 12× regret from ignoring delay against a reactive adversary, delay-tuned rate too cautious on oblivious data, LMSR subsidy ~20× at mean delay 5.
Capacity-constrained expert routing as a congestion-priced market: softmax with dual prices, verifier-computable duality-gap certificate from prices alone, sign-update balancing has a ≈2.5/√B sampling floor plus a step-size limit cycle, closed-form two-expert price of balance, Hoeffding load audit.
Fractional-Kelly wealth markets as expert routers: risk-tolerance-weighted price, ln(1/s)/λ regret bound, growth-optimal λ*=(π−p)/(q−p), manipulation cost V·χ² vs LMSR b·KL (7.5× stiffer at p=0.99), and a switching-truth trade-off where λ≈0.1–0.2 beats full Kelly 3–7×.
Top-k MoE routing as a capped Hedge market: price min(1, λ w_i) with exact KL projection, regret vs the best fixed k-set held under k ln(N/k)/η+ηTk/2 in every run (41–58% of it), plain normalisation prices experts above 1 (282/300 rounds, loss understated 3.2×), and systematic sampling gives exactly k distinct experts with 8–14× lower variance.
A self-financed wealth ledger for specialist modules that sleep: total wealth conserved exactly, sleeping wealth frozen (one private ledger per regime), regret ≤ ln(1/π_i)/η + η·n_i in the module's *own* awake time, entry of a module with wealth ε costs incumbents ln(1/(1−ε))/η; matches the regime oracle (0.1004 vs 0.1000) where forced-to-report Hedge sits at 0.30 and fixed share is worse.
When may a module choose to sleep? The ledger pays exactly leave-one-out savings ηW_A(1−p_i)S_i; sleeping *after* seeing losses gains wealth ηp_Bθ(1−θ)/2 (best 1/8) and takes the market in ~130 rounds with the router's loss unchanged; committed *before* serving it is a real saving; the deterring tax ηp_B/2 is a fixed share that halves honest specialists in 6 rounds.
Conditional markets that route between models: inverse-propensity Brier is proper even when the router reads the report, exploration costs exactly 1+(K−1)e^{ω²/2τ²} in payment variance (probit: infinite for τ ≤ ω), and a stake gap distorts the reported gap by a closed-form fixed point with second-order harm.
Admitting new modules to a Hedge/LMSR router: regret certificates obey a Kraft identity Σ e^{−c_i}=1, so uniform entry 1/(n+1) is the unique minimax rule; prior-optimal shares P_j/S_j cost H(P); the price of entry is exactly ln(1/π)/η independent of the quality gap.
Does bilateral or multilateral netting, or gridlock resolution, save a payment system liquidity? A simulator fitted to Bech and Soramäki's Danish and Finnish bounds (34.7% and 10.1% of gross value against the published 37.2% and 10.7% for DK) shows reciprocal flows are what make netting work, and resolution cuts delay by 24–46% in the Danish-shaped system but 34–62% in the Finnish-shaped one, where the paper found about 10%.
Solomon RC208 (100 customers) with a battery: keeping the battery-blind routes and adding charging stops costs 28% more distance at 150 range units, a charge-aware search brings that to 5%; the battery is harmless above 200 units.
Liquidity, fees, privacy and manipulation in the LMSR markets that aggregate verifier beliefs. Topic page →
LMSR with time-varying liquidity as anytime Hedge: b_t = c*√t costs exactly √2 over the horizon-aware bound, doubling is 1.70× worse, and self-tuning liquidity makes the subsidy equal the accumulated mixability gap (1.3 vs 102 on easy data).
Differentially private LMSR via the binary-tree mechanism: path-wise loss bound, and the accuracy/subsidy cost of privacy.
Manipulating an LMSR verification market: manipulator loss b·KL(q‖τ) equals the extra informed rent, and manipulation raises accuracy only in a liquidity band (thin: costs 1−2q; deep: neutral).
Sandwiching an LMSR verification market: attacker profit is exactly the victim's slippage tolerance times its fair cost, needs capital ≈ εb/(1−p), dies to a fee ≈ v(1−p)/(2b); pro-rata batching keeps 99% of the extraction, random ordering cuts it 3×.
Glosten–Milgrom vs LMSR for a verification market: informed share fixes b* = 1/(2 atanh m) (verified to 2e-16), peak misspecification regret is scale-free and overconfident b costs 1.5–2.4× more, LMSR subsidy → b* ln 2 is the spread GM charges.
Proportional fees on an LMSR verification market: exact no-trade band [q/(1+f),(q+f)/(1+f)], price lag q/(1+f), dead-market cliff f ≥ 2a−1 (threshold 2 atanh f at ½), exact fee revenue f·b·ln((1−p₀)/(1−p_T)), and a break-even fee that costs +38% Brier error.
Sequential LMSR seat rents are conditional mutual information: they telescope to the maker's expected loss (≤ b ln 2), fall with position at the Chernoff rate, order only redistributes a fixed total, and entry costs make error fall only ~1/b in the subsidy.
Convergence of cost-function markets with partially informed traders as randomized subspace descent: maker loss telescopes to ½(e₀'Ae₀−e_T'Ae_T), closed-form slowdown from correlated securities (31→356 rounds at c=0.95, d=5), A-conjugate bundles restore 1−1/d exactly, noisy-belief step size is an SGD step (running mean beats best constant step), LMSR simulation checks the local rates.
Constant-product AMMs as cost-function prediction markets: worst-case loss C0 never attained, informed-trader profit exactly C0(1−n·GM(π)) (ratio to LMSR → ln n, crossover at n=e), polynomial price tails (p=0.999 costs 3.4× LMSR), exact regret identity, no forgiveness gain under regime switches.
Buying compute, data and model improvements: holdout markets, Shapley payments, contests and races. Topic page →
Paying for model improvements against a hidden holdout: telescoping budget, a payment-feedback overfitting attack (paid 0.15 while true loss worsens 0.37), and the Ladder fix with its measured cost.
Shapley and leave-one-out payments under replication: Shapley pays every extra copy even when worthless, saturating at stand-alone value ((n+2)/2× honest), naive evaluators hand over the pot, LOO pays copies 0 but distributes 1/(n+1), dedup underpays lookalikes by 45%.
Auditing sampled Shapley payments: exact estimator variances in a saturating game, permutation sampling is exactly efficient but stratified sampling has 6–8× lower variance (zero for equal contributors) at up to 7% budget error, antithetic reversal gives 1.6× lower RMSE, Hoeffding sample counts are 4–5× conservative.
Winner-take-all training contests scored on a noisy holdout: effort V a_n √m/s with a_2 = a_3 = 1/(2√π) exactly, a precision ceiling V/σ² ≤ λ_max(n) beyond which no pure equilibrium exists (below the zero-rent limit), and the resulting optimal holdout size.
Buying k units of decentralised compute by reverse auction: exact VCG payment k(k+1)/(n+1) is exactly 2× winners' cost, optimal reserve is exactly v/2, first-price equilibrium matches by revenue equivalence.
Paying the first k of n finishers makes speed a contest: π'(1)=(1−k/n)(H_n−H_{n−k}), equilibrium speed R(n−k)(H_n−H_{n−k})/(nc), exact round time nc/((n−k)R); paying all finishers buys no speed, a budget favours winner-take-all until an accuracy floor k_min binds, and recruiting more workers barely speeds the round.
Paying the first k of n finishers when costs differ: proof of the π'(1) telescoping identity, exact exit rule (slow workers idle iff c_s/c_f ≥ n_f/(n_f−k), never for k ≥ n_f), cost ratio 4 excludes slow workers for k ≤ 3 of 4 fast, convex costs make headcount buy speed.
Buying private data with a telescoping log-score market: payment equals information, best Gaussian-mechanism noise in closed form, participation iff κa<1 so precision is capped at λ/(cΔ²) for any number of contributors, and early arrivals over-collect (1–22% welfare loss).
Gossip, local SGD, pipelines, checkpoints and shared rollouts on unreliable, heterogeneous workers. Topic page →
How far over its limit can a rate limiter be pushed in a true rolling window? Adversarial search over fixed window, sliding log, sliding-window counter, token bucket and leaky bucket: only the sliding log holds the limit; the sliding counter admits up to about 1.5 L and the buckets nearly 2 L, and under Poisson overload at 1.5x load 39-47% of rolling windows exceed the limit for fixed window and buckets. Stylised.
Pairwise gossip for decentralised training: exact contraction (n−2)/(2(n−1))≈½ per matching round (~20 rounds at any n), noise floor (n−1)(n−2)s²/n, one stubborn node captures consensus at rate 1−1/(n(n−1)), trust-region clipping caps drift at τ/(n(n−1)) per step.
Local-SGD/DiLoCo-style averaging on heterogeneous quadratics: exact fixed point with saturating weights 1-(1-ηa_i)^H, non-monotone bias to the unweighted mean, exact a_i/w_i correction, step-count inflation moves the fixed point 0.50→0.91, wall-clock-optimal sync interval.
Checkpoint interval for preemptible decentralised training: exact Lambert-W optimum independent of restart cost, Young/Daly overshoot 5–25%, flat within 2×, synchronous efficiency wall (50% at n≈691), flaky workers cut throughput 5×.
Replicate or skip? pipeline stages on unreliable workers: exact binomial drop law, replicas cannot beat the shared-domain floor (1−ρ)^L, a 4-stage skip budget halves workers for a 1e-3 drop rate (240 → 96), cost-optimal design shifts from skipping to replication as skips get costly.
Cutting a model across heterogeneous devices: exact greedy bottleneck partition (matches DP, with memory caps), W/V ≤ T* < W/V + m·w_max/V, speed-blind splitting costs exactly v̄/v_min (2.4× at σ=0.5), device order is the residual decision (sorts no better than arbitrary, swap search within 1.1%), memory inverse to speed costs 1.7×.
Waiting for the fastest k of n workers: exact order-statistic round times (Pareto mean finite iff n−k+1 > 1/α), exact SGD time-to-accuracy with a minimum k and an interior optimum (34× over wait-for-all at s=0, 1.12× at s=32), joint step tuning, and the exact selection bias of the speed filter with Horvitz–Thompson correction.
Rollout sharing in swarm RL as a public-goods game: Nash gives every agent a lone agent's learning level whatever N (total effort caps at (a/c−1)/θ) while efficient welfare is 4.5× at N=256; at θ=1 one agent generates; a Pigouvian matching subsidy (fraction θ(N−1)/(1+θ(N−1)) of cost) implements the optimum; junk beats honesty iff c−ε > p(τ+F).
Stale off-policy rollouts in swarm RL: exact importance-weight moments (E w²=e^{δ²}, ESS fraction e^{−δ²}), closed-form truncation bias/variance verified by simulation, best cap cuts shift-estimation MSE 1.9× at δ=1 and ~750× at δ=3, and the staleness window √ln(1/ρ)/drift.
Exact catastrophic-forgetting law for sequential training on random low-rank tasks: (r/d)(1−r/d)(ρᵏ−λᵏ) rises then vanishes, uniform module routing dilutes it but sharing wins on seen-plus-fresh loss, conflicting tasks leave a floor 2rτ²/d.
Merging independently trained modules on random low-rank tasks: exact residual 1−2amp+a²(mp+m(m−1)p²), optimal scale 1/(1+(m−1)p) (averaging stalls at (1−p)², unscaled sum diverges), harmonic 1/m decay, parallel speedup only logarithmic (8.9× at m=16, d/r=8).
Exact expected forgetting under replay schedules in sequential training on random low-rank tasks: 2×2 matrix recursion matches simulation, one replay is best at the forgetting-peak lag yet removes only 25–42%, a fixed period beats random replay only below ~1.2–3 peak lags, halving forgetting needs rate 0.25 (d=12, r=3) to 0.015 (d=128, r=1).
Partial replay when only m of an old task's r examples are stored: exact 2×2 law interpolating no replay and full replay, best-step saving nearly linear in m/r, and at a fixed example budget a few large replays beat many small ones by only 0.1–6 points.
Task-aware routing when continual-learning tasks conflict: the long-run floor is (2r/d)[τ_w²+τ_b²(1−Purity)] with purity = 1 − the router's Gini impurity, random modules buy nothing, a perfect router removes (m−1)/(K−1) of the between-cluster floor, and a 10% routing error gives back 36%.
DiLoCo-style outer momentum: H inner steps precondition the outer quadratic (κ_H ≈ κ/H), exact per-mode rates, optimal momentum falls 0.88 → 0.01 with H (fixed 0.7/0.9 Nesterov needs 4–8× more rounds), and the wallclock-optimal sync interval is H* ≈ C (sync cost in inner steps), worth ≈ √C/2.
Noise floor of DiLoCo-style local SGD: exact stationary loss αV(1+β)/((1−β)s(2(1+β)−αs)), independent of H at α=1, momentum free at equal effective step, near-linear speedup in M, and a noise-limited sync interval that grows as the floor target falls.
Local SGD when workers drop in and out: exact floors for participant averaging (E[1/K|K≥1]) and expected-count normalisation (stable iff αsc<2), at matched speed the fixed normaliser is quieter by E[K]E[1/K] at small steps, and reliable workers bias the fixed point unless inverse-propensity weighted.
Local SGD with compressed displacements: exact floor (1+ω) and stability limit αs(1+ω/N)<2 for rand-k (more workers restore the step, not the floor), closed form for norm-scaled quantisation, and at equal bytes syncing less often beats compressing.
Overlapping communication in local SGD with τ-round-late outer updates: exact stable step 2 sin(π/(4τ+2)) (shrinks ~1/τ), double-root rate τ/(τ+1), exact noise floor matched to simulation, free at small steps, wall-clock-optimal delay ⌈L/T_c⌉ (1.9–7.5× faster than no overlap).
Error feedback in compressed local SGD: exact stability limit 2(2−ρ)Nρ/(Nρ²+4(1−ρ)) and closed-form floor that returns to the uncompressed one at small steps (unbiased compression pays 1/ρ), dropping is biased to the send-rate-weighted mean and the residual removes it at a variance price.
Weighting workers that ran different numbers of inner steps: exact floor α²Σw²V/(r(2−r)), worker information I∞·tanh(λH/2) saturates, optimal weights span ≤2× so equal weights lose ≤9/8 (measured ≤1.09) while step-proportional weights lose up to 1.76× per mode and 10.5× on three modes.
Median and trimmed-mean outer aggregation in local SGD: exact linear loop with floor and bias split, π/2 variance price with no attackers, bounded worst-case bias Φ(z)=1/(2(1−ε)) that more workers cannot average away but a longer inner loop shrinks.
Research programme (proposal stage): a predictive theory of DiLoCo-style low-communication training, testing on real small transformers the closed forms derived in about a dozen quadratic-model projects, with 16 references, hypotheses H1 to H6 and an ICML/NeurIPS workshop as the first target
What a simulated clone of a physical system is worth for training and validating controllers: transfer regret, validation, and randomization. Topic page →
Gaussian-depth-noise stereo twin vs real disparity-space noise: median exact, gated mean biased by ≈s², over-range errors up to 191× more frequent at 40 m, a twin 3σ margin exceeded 10× as often, mean-depth averaging floors while averaging disparity converges (negative result at the 60 m range floor). Stylised.
A rigid twin of a cart carrying liquid predicts zero slosh: minimum-time move leaves 10.7 cm (10× tolerance), slosh-safe move is 55% slower, and a full-tank frequency calibration fails at low fill (28 s vs 8.7 s recalibrated; tuning-free bound 24.7 s).
Input-shaped moves of a liquid-carrying cart: ZV/ZVD residual sin(πε/2), sin²(πε/2) exactly multiplies the bang-bang residual, so a stale frequency calibration that breaks the null-tuned move (28 s) is harmless to a 5.9 s ZV move; closed-form tolerated error and a fill-band design that spends the tolerance on a shorter shaper.
What a digital twin is worth for training a controller: exact LQ sim-to-real regret with a stability cliff, a validation blind spot (zero score gap yet mistrained control without probing), and a twin worth exactly σ²/(vδ²) real samples at any accuracy.
Domain randomization over a twin, exactly: cliff-limited width, quartic price when the twin was right, cliff pushed out ~15%, but uniform-average training is not minimax and the best width tracks the prior.
Keeping a digital twin in sync with a drifting plant: closed-form Kalman tracking variance and control regret (matched to simulation), a frozen twin loses half its edge in ln 2/(2(1−ρ)) steps, probing never pays for one drifting parameter, and a two-parameter closed-loop blind direction gives a mean-field dither law ν* ∝ q^{1/6} that self-exciting certainty-equivalent control mostly makes unnecessary.
Re-identifying a drifting twin by dedicated experiments: closed-form interval T*∝q_d^{−2/3} with downtime, noise and drift regret exactly equal at the optimum, excess ∝q_d^{1/3}, a 4× drift misjudgement costs ≤26%, but the second-order optimum destabilises 0.7–15% of cycles and a safe schedule is 37–200× worse than an always-on Kalman twin.
What to pay a digital-twin provider for: cost-paid twins differ from Brier-paid ones, certainty-equivalence loss is quartic in spread, payment caps make the elicited twin jump at a closed-form threshold, and Brier mispays probing by 15×.
Anytime-valid e-process audit of a digital twin in closed loop: peeking-safe (2.4% vs 58% false alarms), delay set by the controller's own excitation, regret before detection nearly independent of the gap, dither pays only for gross errors.
What a Gaussian-clutter radar twin does to a CA-CFAR detector: exact false-alarm law under gamma texture (matched to simulation), 9–30× inflation at design 1e-4, 1.9–3.7 dB threshold repair, shared texture is harmless, and a real-cell calibration budget (median 1.1× at 1000 cells).
Does a more robust CFAR survive a Gaussian-clutter twin? CA, OS and log-t all inflate 8–44× at design 1e-4 (no detector escapes), a known-scale oracle inflates as much as CA (the test cell's own texture), and CA detects best at equal real Pfa after repair.
When a collaborative robot should give up waiting for a human: J'(τ)=S(τ)(w−c·h(τ)) makes exponential/Weibull simulated humans corner-only (never abort), 3.7% regret in the base case rising to 37–81% for heavy tails and cheap aborts, plug-in lognormal fit regret 1/n (delta method within 11%).
What a too-clean sensor twin does to a mapper's commit error: exact real error via the Lundberg exponent (false-hit 0.05 twin vs 0.15 real turns 1e-3 into 1.45e-2, 14.5×), tempering restores the target at 1.4–16× latency, and the exponent needs several hundred real samples to estimate.
Cloning an expert from twin-logged demonstrations under actuator saturation: applied-action logs bias the clone even in a perfect twin (gain 0.58 vs 0.96, +9.8% cost), Stein closed form, quieter or looser twins help, narrow coverage fixes it, DAgger with applied labels is worse.
Cloning a privileged teacher from a digital twin into a noisy-sensor student: BC gain gP/(P+s) is set by the twin's noise-to-sensor ratio, a too-clean twin (¼ the noise) gives 0.36–1.11 excess cost vs 0.005–0.10, on-policy imitation is within 3.5% of optimal, cancellation with actuator error is accidental, and matching one real scalar by demonstration noise fixes it in two rounds.
What a twin without sensor latency does to a tuned controller: exact stable-gain interval shrinks with delay, the zero-delay LQR gain tolerates one step (1.6× cost) and is unstable from two, retuned static gains cost 1.1–2.6×, wrong-delay predictors are mostly unstable, and delay identification needs ≈2z²(1+1/snr) samples.
UAV targeted observation planned in a forecast-ensemble twin: exact real error after twin-gain updates, a 2×-too-long correlation length claims −65% and delivers +28% (closed-form harm radius), 10 correct-model members already hurt, localisation and a fitted length scale (m≈50) repair it.
What a deterministic-duration twin of a lab workcell promises: exact expected max of gamma branches, 1.86× promise miss with exponential branches (3× at the 95% quantile), station count under- or right-bought depending on how variability scales, and ~5 real durations fix the decision but ~50 the makespan.
How firmly to grip in a friction twin: closed-form (quadratic) optimum force under slip vs crush, a twin with spread 0.1 vs real 0.3 claims risk 1e-5 and delivers 0.069 (4× the optimum, 11.6× at 0.05), a zero-spread twin has no unique policy (real slip 0.50 to 0.015), width can cancel a known bias but not an unknown one, delta-method calibration budget.
Battery reserve of a UAV leg planned in a constant-wind twin: cruise speed nearly right (regret 0.1%) but the energy claim is low by exactly artanh(x)/x (3.5%) and a battery sized to it depletes in 50% of real flights; 5% depletion needs a 39% margin, and the twin speed stalls once wind spread exceeds v−μ.
A SLAM loop-closure gate tuned in a too-clean odometry twin: exact chi-square gate costs and closed-form optimal gate, real noise 2× the twin's rejects 38% of true closures (claimed 2%) at 4.4× the claimed cost, pessimistic twins are not safe either, and ~59 ground-truthed closures repair it.
A chi-square loop-closure gate tuned in a too-clean odometry twin: exact real error 2.1× the claim at drift-sd ratio 2, rejected genuine closures compound into lock-out (9–16× the ungated error, growing with horizon), the gate halves aliasing error when the twin is right but is 8× worse than no gate when it is not, and ~30 measured drifts make the repair safe.
How often a mapping team should rendezvous when its twin's odometry drift has no bias: real error is exactly √(1+ρ) times the claim, cost-optimal interval solves a cubic, twin regret 0.19–34.6%, shared bias cancels in the pairwise frame (5.3%→0.10%), and repair needs a long-lag ground-truth fit.
A twin tuned on one-step odometry noise cannot see drift: variance ratio exactly 1+(T−1)ρ, relocalisation interval 3.4× too long (real miss 51.6% vs 5%), twin-tuned loop-closure gate recall 0.64 at T=200, closed-loop runaway, aliasing limits calibrated gates.
A corridor-keeping safety margin certified in a Gaussian-disturbance twin: same variance, heavy-tailed real gusts give 0.29 real failure at a claimed 0.01, needed margin 7.3× at δ=0.001 (ν=3), variance inflation misses by 24×, conformal needs n≥1/δ, a Hill tail fit from one-step data repairs it.
A lidar twin with i.i.d. beam dropout certifies the thinnest detectable obstacle: real clustered dropout (same rate, lag-1 correlation 0.6) misses 41× more at the certified width and the range claim is 4× too long (exact Markov miss law, p·q^(m−1)); a fitted persistence recovers the median width but needs a margin.
Can a twin shorten a real-world safety certification? Worst-case size of any k ≤ c rule is exactly P(Bin(n,ε) ≤ c), so a twin prior cannot cut real trials at a fixed level (299 exact zero-failure trials; twin prior reaches 133 only at size 0.26); wrong twins inflate size or block certification.
The cost a planner quotes from its own twin rollouts is optimistic by exactly e_K·s (winner's curse; 95% intervals cover 60% at K=20), fresh rollouts fix the sampling part at a selection-quality price, but not the twin's own model error −e_K τ²/√(τ²+s²).
How many retries a grasp needs when the twin treats attempts as independent: exact Beta-mixture failure law (power law k^{−a} vs geometric), twin budget 6 claims 0.004 and delivers 0.010–0.151, real budget 7–571, closed-form give-up rule, and a two-attempts-per-object repair that still needs a margin.
The best of K controllers picked in a noisy twin: winner's claim optimistic by exactly τ²c_K/√(v²+τ²) (c_K=E max of K normals), under a fixed rollout budget more candidates can make the deployed one worse (best K=5–22), an exact-plant LQ twin's claim falls below what any gain can achieve, and screen-then-verify cuts claim bias 4.5×.
Evaluating a robot policy with a biased twin as a control variate: unbiased whatever the twin's bias (+0.700 twin-only vs +0.001), exact variance σ²((1−ρ²)/n+ρ²/N), ρ=η for a faithful twin but √η for a noise-free one (1.33× vs 2.0× real-sample gain), worth-it threshold c_T/c_R<(1−√(1−ρ²))²/ρ² (0.072 at ρ=0.5), and 86–125 vs 164 real episodes per policy to rank correctly when twin bias favours the wrong one.
How big a pilot decides whether a biased twin is worth using: threshold ρ*=2√r/(1+r) with a gain linear in ρ−ρ*, so wrong calls are frequent but cheap (regret 0.004–0.016 at ρ=0.5), decision-regret law f·slope·(1−ρ*²)²/(2m) (ratio 0.63→1.00 for m=10→160), plug-in allocation ≈0.27–0.30/m, and an adaptive two-stage design that stays unbiased (|bias| ≤ 0.002) with 0.946–0.955 coverage.
Seed-paired (common random numbers) policy comparison in a twin: correlation is exactly lost to random-stream desynchronisation (flat score 0.95→0.77, terminal score 0.36→0.001 at q=0.05→0.3), a sizing trap (power 0.11–0.85 vs nominal 0.90), and counter-keyed draws restore ρ=1.
What overshoot a controller tuned in a fixed-step twin really has: exact per-step decay laws for explicit/semi-implicit/implicit Euler, damping bias flips sign at ζ=1/√2 (explicit, implicit), a 10% twin target delivers 0.105–0.192 real overshoot (implicit/semi-implicit) or 0.036–0.091 (explicit), error first order in h, Richardson repair.
A too-narrow scenario generator in a twin makes rare-failure estimates silent: reweighted variance finite iff s²>½, 0.6× width claims 2e-7 for a real 1.2e-3 and reports zero failures in all runs, optimal width ≈1.05·a needs 38× fewer runs than plain Monte Carlo, and a defensive real-prior mixture is finite but no better.
An estimator tuned in a twin with wrong noise levels: exact real MSE of the twin's Kalman gain, optimistic claim when the twin is too quiet (+121% at 10×) vs pessimistic when too noisy, no instability cliff, and a Mehra innovation retune with regret ∝ 1/n.
A controller designed in a twin with the wrong actuator gain: exact real LQR cost, an instability band the twin does not warn about, closed-loop non-identifiability without dither, and a dithered retune with matched regret law.
A limit-free twin of an unstable plant with a saturating actuator overstates mean time to loss of control by 6,295× at noise sd 1 (1.5×10⁶ vs 245 steps), an exponential-in-1/s² gap (slope ≈3.7 real vs ≈12.7–13.2 twin), though both rank the deadbeat gain best.
A Kalman filter tuned in an ideal-sensor twin, run on a quantizing sensor: twin gain costs +11% (R=1, D=4) to +64% (R=0.01), Sheppard R+D²/12 retune is within 1% of best, but its MSE claim under-predicts by up to 43% once the step exceeds the state's scale.
Splitting a simulation budget across twin fidelities (multilevel Monte Carlo): smooth quantity saves 3.6×–897× (rates α=1, β=2), a failure probability only β=1 so multilevel loses at loose targets (0.4×) and reaches 7.7× at 1e-4; equal samples per level cost 156×/3.9× the optimum.
Fine-tuning a twin-pretrained policy on the real plant: exact SGD risk, a twin start saves 64–67% of real steps at 0.6× the cold error but is negative transfer beyond 1×, and twin error decays only as b²/(4eηk) (flat directions inherited: 13 vs 1,541 steps at equal initial loss).
How far ahead a controller planned in a wrong-pole twin should look: exact real cost per horizon is non-monotone when the twin overstates the pole (1.81 at H=2 vs 3.97 at H=60, optimum 1.48), the twin's own claim ranks horizons backwards, exact two-step stability edge, and a Riccati terminal cost removes the effect.
Mixing cheap biased twin samples with scarce real ones: exact optimal weight, twin worth capped at σ²/δ² real samples, equal pooling helps iff δ²<a+b, and estimating the bias from data is costly (plug-in worse than real-only for large bias).
How much load a shared lab instrument carries when its twin assumes exponential service: exact Pollaczek–Khinchine wait off by (1+c²)/2, twin admits ρ=0.667 vs real 0.444 (c²=4) or 0.133 (c²=25), tails 11.7× worse, infinite mean wait for Pareto index < 2, and a plug-in c² repair that violates the SLA 70–89% of the time.
Smoothing a hard contact edge to make a twin trainable: real gradient is zero, twin ascent is trapped below τ_c=0.105 and misses the edge above R/(8cm), annealing crosses the trap, and the overshoot ≈τ ln(R/(2cmτ)) is an implicit safety margin capped at 0.168.
How many redundant sensors a twin with independent errors says a robot needs: exact equicorrelated fused variance, n_eff < 1/ρ and a floor σ√ρ, twin says 16 sensors vs real 30 (ρ=0.03) or none (ρ≥0.0625), 3σ gate false-alarms 8.6× too often, and a plug-in ρ repair that misses the target about half the time.
How much one long digital-twin run is worth when its output is autocorrelated: exact AR(1) run-mean variance, M/M/1 wait inflation 9.7×–363× (ρ=0.5–0.9), naive 95% intervals cover 9–53%, false SLA certification 26% vs 4.8% with batch means, and batch means fail when batches are shorter than the correlation time.
A twin started in the wrong state: exact AR(1) warm-up bias and MSE-optimal deletion (≈ one relaxation time, ≤1.5× gain), M/M/1 empty-start bias (−21% at ρ=0.9, n=500; 1% at 10⁴), and a negative result: MSER-5 truncation leaves more bias and more false SLA certifications than fixed deletion.
A twin with Gaussian range noise vs real non-line-of-sight bias: exact rms law GDOP·√(σ²+p(2−p)m²) (4.5–7.3× the twin's error, zero mean), a predictable bias for a blocked side, anchor counts 4 → 28–46 for a 1 m / 95% corridor, and a trimming fix that costs 24% when NLOS is absent.
A twin identified from logs of the deployed controller: held-out error is 1.00σ² at every dither level while the predicted pole under a new gain has sd (σ/√n)√((k−k')²/τ²+1/v) (0.037→0.82), no dither gives a confident wrong twin (b̂=−0.22 vs +1), point-rule false stability certification 3–48% vs 0.1–4.7% for the OLS bound.
A twin fitted to finite real data: exact delta-method error √(1+(2−ρ)²)/((1−ρ)√n) of its steady-state wait, data needed grows as (1−ρ)⁻² (22 100 per stream for 10% at ρ=0.9), exact instability probability, false SLA certification 36–46% fixed by bootstrap/posterior bounds (delta bound under-covers).
Real data or more simulation for a fitted twin: relative variance a(ρ)/n + b(ρ)/m (matches simulation), one real pair ≈ 2 simulated jobs at any load, optimal real-data share 0.57–0.97 by cost ratio, and a simulation-only interval whose real coverage falls 0.79→0.17 as the run lengthens while the input-aware one stays 0.92–0.95.
When to stop a twin run counting rare failures: sequential Wald stopping halts on zero failures (90% of runs at p=10⁻³, coverage 9.6%), inverse sampling to m failures gives exactly unbiased (m−1)/(N−1) with relative sd ≈1/√(m−2) and an exact interval (95.0–95.5%), while a fixed run planned for the wrong p delivers 63–200% half-width.
Stopping distance certified by a twin with independent per-cell friction: exact incomplete-gamma law (matches braking simulation), 100 twin cells certify 1.17× the mean distance but real terrain with 1–10 patches exceeds it 44%–18% (claimed 0.1%), finer cells are worse, the mean is nearly right, and the measured patch count repairs it.
Approach speed certified by a lidar twin with independent beam dropout vs real whole-scan fades: exact scan-product miss law, real miss ~100× the level at the twin's speed, speed off 10–30% (probabilities off by orders of magnitude), sign reverses when several returns are needed, repaired by a few hundred calibration scans.
Importance sampling of a rare twin failure: exact mean-shift variance, 10⁸→535 runs for 10% error at p=1e-6, a narrow shift target (2× the optimum is 1.7·10⁵× worse, 0% coverage) and effective sample size as the only warning.
Radar ego-velocity from Doppler returns: a static-world twin picks least squares, but with moving targets its variance is exactly 1+ετ² times the claim (95% interval covers 48.7% at ε=0.1, τ=10) and the median wins on a band of ε (0.006–0.97 at τ=10; never at τ=1).
A radar twin with no Doppler folding: the twin-tuned ego-speed estimator breaks at v_u−2σ with an exact closed-form bias (saturating at one fold off), and a wrapped-cost search unfolds it iff azimuths are diverse, with a confusion probability Φ(−√E₁/2σ) matching Monte Carlo.
Validating a twin's rare-failure rate against real trials: an exact difference test "passes" a 3×-wrong twin 81% of the time at 500 trials, rejecting a 2× error needs ~11 real failures (any q), and an equivalence test needs ~20/58/178 failures for margins 2/1.5/1.25 (~20/q trials).
Goal inference tuned against a simulated human: exact real error 1/(1+r^h) of a commit threshold, 3.9×–165× over target for a too-rational twin, 2–4.5× slower for a too-irrational one, population floor P(p<½), and calibration from n real cues misses the target 14–42% of the time.
Sensor clock offset and jitter a twin does not simulate: exact added variance 2σ²[1−(1+s²/ℓ²)^{−½}e^{−δ²/2(ℓ²+s²)}], a synchronised-clock fusion design is 1+ag/(b(a+b))× its claim (+44% at 0.3ℓ) and worse than one sensor beyond 0.225ℓ, better delayed sensors hurt more, clock randomisation fixes it.
A twin gain fitted from a noisy logged input is attenuated by exactly the reliability ratio λ (0.800 vs 0.802 simulated), more data makes the twin's own 95% interval worse (covers the true gain 53%→0% for n=20→200) with no residual warning, a feedforward controller overshoots by exactly 1/λ, and known-noise or instrument repairs cost variance and fail at small n.
An actuator deadband the twin lacks: real loop rests at exactly d/k while the twin goes to 0, tolerance ε needs k ≥ d/ε, a fitted linear gain is 2Q(d/s) (excitation-dependent, small-signal gain 0), and bisection compensation leaves exact (d−d̂)/k or a (d̂−d)/(2−k) chatter (8 probes: 0.784 → 0.0005).
Follow-up to deadband-twin: measurement noise flips the linear twin's error from 27× optimistic (s=0.01) to conservative (0.37× at s=0.05), dither helps only without noise, and mild under-compensation beats the exact width under noise (single-seed simulations).
A twin without an actuator rate limit is exact only for x₀ ≤ r/k; beyond it the real loop overshoots (0.90 of x₀ at x₀/r=10⁴) and settles in O(amplitude) steps, with an empirical overshoot threshold 2n(2n−1) for k=1/n.
A rigid-drivetrain twin says the PI loop converges but gear backlash makes the real loop hunt at 1.3–2.9× the gap (exactly ∝ h); describing-function prediction 7–10% high, and bistable starts can hide it.
A viscous-only twin never stops (6.5–17.7 s to reach 1e-3…1e-9 vs 1.95 s real) and its fitted gain b + c·E[v]/E[v²] depends on the logged speed range; fitted on [1,3] it overestimates stopping distance ×1.8–17 below and underestimates above v*=7.3, no single viscous gain beats 0.87 worst error over [0.05,3], affine fit recovers exactly.
A twin with the right sliding friction says the PID loop converges, and with no stiction it does; a breakaway excess Fs−Fc makes the real loop stick-slip hunt at ≈0.5–0.9 ΔF/kp (independent of Fc), and short runs can mistake a long stick for convergence.
A twin with an instantaneous actuator is stable at any gain; the real loop with lag τ is stable iff τ<kd/kp=2ζ/ωn, hunts at the twin's own ωn, decays no faster than 1/(3τ) for any gains, and the real-optimal bandwidth is ≈0.26–0.46 of the limit.
A rigid-body twin certifies every PD bandwidth; with load-side sensing the real two-mass loop is unstable above ε_c ≈ δ/ζ of the flexible-mode frequency (exactly independent of mass ratio, unstable at any gain with no modal damping), step-response validation misses it, and the certified bandwidth inherits modal-damping error one-for-one.
A per-axis twin of a two-axis loop certifies gains that actuator coupling destabilises: stable-gain limit 2/(1+√p) not 2 (a 10% margin fails at c=1/9), twin-deadbeat rate is √|p| not 0, and a fitted diagonal gain 1+cρ depends on log correlation while the full fit's variance grows as 1/(1−ρ²).
A twin with an unlimited actuator is exact for a PI step only while kp·x0 ≤ U; beyond it the integrator winds up to x0²/(2U), overshoot rises from 21% to 97% and settling from 4.9 to 944, loads d ≥ U are never rejected, and the twin-tuned faster gains settle slower (clamping recovers most).
A fixed-step twin of a bouncing ball: the true rest time (v1/g)(1+e)/(1−e) is hypersensitive to e (2/(1−e²)), the twin's apparent restitution and settling time are off by O(dt) with scheme-dependent sign (−20% to +4% at dt=10⁻², e=0.9), and calibrating e on the first bounce is not a reliable fix.
A twin fitted to the sensor-delay histogram is blind to its persistence: i.i.d. jitter at the mean delay barely moves the mean-square gain limit (1.00 for {0,2}), but with the marginal fixed, lag-1 autocorrelation 0.9 cuts it to 0.67 (0.9 certified by the twin is unstable from ρ=0.435) and inflates variance 2.4×; almost-sure stability (≈1.84) hides it.
A gravity-free twin certifies PD with zero error; the real pendulum sags to the root of kp(θ*−θ)=g sin θ (0.18 rad at kp=4, falling only as ~1/kp), cannot hold upright unless kp>g (basin 0.12 rad at 1.02g), and a 10%-off gravity feedforward leaves a sag linear in the error.
A continuous-time twin certifies PD at every gain; the real zero-order-hold loop is stable iff kp·T/2 < kd < 2/T (ωn·T < min(4ζ, 1/ζ)), overshoot is 5× the twin's at ωn·T = 1.2, raising ωn past ωn·T ≈ 1 slows settling, and deadbeat (2 samples) is the real speed limit.
A linear-drag twin of a quadratic-drag vehicle: coast-down time and terminal speed are off by fit-speed ratios, least-squares fit gives k = 3c·vmax/4, and the safe speed under a stopping limit is mis-stated by −21% to +41% with sign set by the fit speed.
A kinematic-bicycle twin of a car ignores tyre slip: steady-turn radius is off by exactly 1 + Kv²/L (twin 4–63% too small, half at the characteristic speed), calibrating K fixes that but both twins certify steering gains stable at every speed while 11 of 30 real gain pairs lose stability below 60 m/s.
A grid twin over-states every route by a heading-dependent factor that cell size does not shrink (8-connected: mean 8(√2−1)/π = 1.0548, worst 1.0824 at 22.5°), calibrating the mean leaves −5.2% to +2.6%, and the twin ranks two routes (lengths 1 and 1.03) the wrong way round 19% of the time; rotating the map flips a fixed pair for 31% of orientations.
A global-shutter twin of a rolling-shutter camera ignores target motion: a moving rectangle is sheared and stretched by exact closed forms, a twin-trained orientation estimate is biased by half the edge tilt (1.79° at 1000 px/s), and one frame of a known-size target identifies pose and velocity (0.027° and 16 px/s at 0.25 px noise). Stylised.
A snapshot-scan twin of a spinning lidar ignores motion during the sweep: length biased by exactly vτ/2 (0.5 m at 10 m/s), parallel walls converge by vτ/2π·(1/d₁+1/d₂), one scan gives speed to 0.13 m/s, yaw scales bearings by −κβ/(1+κ), acceleration biases odometry by a·t_f without accumulating.
A white-noise satellite-positioning twin vs a receiver with correlated multipath: exact HDOP √(4/n) and bias map 2b/n, averaging loses the 1/√T gain (95% radius covers 33% at T=10, 5% at T=100), and a residual integrity test tuned on the twin false-alarms 21% at equal multipath. Stylised.
Point-mass twin of a rolling body ignores rotational inertia: acceleration overstated by exactly 1+k, slip threshold k tanα/(1+k) invisible, coast distance 40–100% off, one calibration cannot fix a mixed fleet.
A pinhole twin of a radially distorted camera mis-ranges the floor by exactly 1/(1+k₁h²/R²) (+8.1% at 1 m for k₁=−0.3), a twin-trained braking policy stops 9 cm short of 1 m, focal calibration trades the near-field error for a far-field one, and one grid image identifies k₁.
An instantaneous-exposure twin of a finite-exposure camera certifies detection at every speed; a moving bar is an exact trapezoid (peak C·min(1, w/d)), a twin-tuned peak detector has a hard speed limit wC/(σz), and a blur-matched box filter raises it quadratically (5–55×).
A twin with an ideal magnetometer hides hard/soft-iron heading error: exact peaks asin(β/B) and asin(|1−r|/(1+r)), a compass-held square misses by exactly 2Lβ/B, and swing calibration error grows ×12 at a 90° arc. Stylised.
A gyro twin calibrated on white noise hides the bias random walk: heading variance ratio exactly 1+(t/t*)² (2.33 at 100 s, 134 at 1000 s), the twin's re-alignment interval is 24× too long (10 000 s vs 416 s), a single-point Allan fit is right at one horizon only, and dead-reckoning range is over-stated 1.25–1.74×. Stylised.
Zero-wind twin of a UAV out-and-back leg: wind does not cancel (real/twin energy 1/(1−(w/v)²)), the best airspeed moves to v²=w²+√(w⁴+1), and a one-leg-calibrated twin is off by exactly ±w/v with the sign of the leg flown.
A constant-gain twin of a motor holding a load certifies every load: magnet derating makes holding a positive thermal feedback with a fold at λ=4/27 (real temperature 1.33–2.25× the twin's near it, no hold above it, runaway in ≈4π/(9√ε) thermal time constants), short tests cannot see it, the twin overstates holdable torque 1.1–1.6×, and refitting a constant gain does not remove the fold.
A twin whose sensor reads at any distance vs a range-limited one: exact step-count law (49 vs 4021 steps from 1000R), PI overshoot neither bound nor lower bound (4.1× at 1000R), exact scale invariance, and the gain fitted from logs of a given extent.
One long twin run or many replications under a start-up transient: exact AR(1) MSE and t-interval coverage (single run minimises MSE; replication costs 1.07×–2.2×; 92% coverage at MSE-optimal deletion for short replications), batch means not worse, preliminary M/M/1 coverage 6–84%.
Cold-start bias of short twin runs: exact AR(1) bias/variance/warm-up deletion, M/M/1 empty-start bias constant ρ/(1−ρ)³, negligible at valid-interval lengths but −5.6 of 9 at 50 jobs; MSER-5 did not help.
Shortlisting K designs in a twin and verifying the top m on the real plant under a fixed trial budget: twin-only value exactly ρc_K, best m falls from 8 to 2 as ρ rises 0.6→0.95 (K=50, B=20), and a useless twin still gains 0.12 from budget concentration alone. Stylised.
Pulling a real-plant parameter estimate toward its twin (James–Stein): exact risk d−(d−2)²E[1/(d−2+2K)], never worse in total for d≥3, perfect twin risk 2 at any d, worth n+σ²/τ² real samples at large d, but one mismatched parameter takes ≈d/4 noise variances (25.5 at d=100) unless shrinkage is blockwise (1.65 at blocks of 5, d=30).
A radar twin assuming the sensor is body-aligned: planar dead reckoning is exactly the true path rotated by the mount yaw (error 2 sin(e/2)·|displacement|, bounded, zero after loops, so loop-closure validation is blind), closed-form rotation fit with std σ/√Σ|p|², but a pitched mount drifts vertically laps·2πR sin e.
Certifying a policy with a biased digital twin: exact twin/plant cost correlation, optimal twin-to-real rollout split and speed-up (matched by simulation), bias first order but correlation second order in model error so the replayable-disturbance fraction caps the twin's value, and twin-only intervals cover ~0%.
What a Gaussian-clutter radar twin promises about detection: exact Pfa/Pd laws for CA- and OS-CFAR in textured clutter, OS inflated like CA, an SNR shortfall (6.3 dB at ν=2) larger than the threshold repair, and no CA/OS ranking reversal.
Estimating a controller's real cost with a biased digital twin as a control variate: cost correlation in closed form (0.985 → 0.472 as the twin's gain error grows while its bias grows 300×), exactly λ² under partial disturbance replay, optimal twin/real ratio √(c_rρ²/(c_t(1−ρ²))) and break-even twin price, simulated variance ratio 0.228 vs 0.225 predicted.
Anytime-valid monitoring of a deployed twin: e-process on closed-loop residuals (2.3% vs 51.6% false alarms under peeking), rate = twin-transfer score gap, an invisible blind line Δa = kΔb that needs dither v, and when dithering pays.
Compressing DiLoCo reports: unbiased compression multiplies the contraction (c = 1+ω/M, stable iff αsc<2, participation is ω = 1/p−1), dithered quantisation only adds Δ²/12 and keeps stability, and at fixed bandwidth quantisation has an interior optimum near 1.3 bits per coordinate (~4× below 8-bit reports) while sparsification favours few full reports.
Sending a fraction p of the outer update: unbiased rescaling costs 1/p in noise floor, error feedback costs only 1+αs(1/p−1) at small steps but caps contraction at √(1−p); exact closed form, stability limits, horizon losses.
Overlapping the DiLoCo sync by applying the outer step τ rounds late does not pay: stable iff αs < 2 sin(π/(4τ+2)), best rate 1−2 sin(π/(4τ+2))/κ_H (exactly κ_H/(κ_H+1) at τ=1), momentum is useless once τ≥1 (69 → 1388 rounds at κ_H=100), hidden-sync gain ≤ (τ+1) sin(π/(4τ+2)) ≤ 1 (search: 1.5–4.9× slower than blocking averaging), fixed if the fresh pseudo-gradient has weight >½.
A twin whose wind gusts are iid per step with the logged variance: real position variance is s²(a+k_d)/(k_d k_p(a²+a k_d+k_p)), the twin's is 141× smaller at a=1, dt=0.01 and scales as dt, its 1e-3 margin is exceeded 78% of the time, and a spectrum-matched white twin is always conservative.
Free-space radar twin vs two-ray ground-bounce lobing: detection fraction exactly 2/3 at the free-space range edge, real detects 44% beyond it, a two-ray twin with height error δh disagrees ≈4h_rδh/(λr) and is worse than free space at short range, a height-jitter ensemble scores Brier 0.119 vs 0.197 deterministic. Stylised.
Point-target radar twin of two unresolved scatterers under ideal monopulse: real mean is exactly the strong scatterer and median exactly the power centroid, outside-span probability arccos(r)/π, a variance-matched Gaussian twin is 27× too optimistic at a 3σ gate (r=0.9), averaging looks floors at bias 2r²/(1+r²) where the twin predicts √(var/N), and the median beats the mean for r≥0.477. Stylised.
Constant-variance Gaussian camera twin of Poisson photon counting: the real Bayes threshold is the logarithmic mean, the twin's the arithmetic mean (7.28 vs 8.00 for 4 vs 12), a detector tuned in it has 1.25–1.83× the optimal error and 23× at λ0=200 (λ1=2λ0), and a square-root twin recovers the optimum in 8 of 9 pairs. Stylised.
Single-cell radar twin vs a real matched filter: exact Rician ghost false alarms (0.020 at 20 dB, 1.0 at 30 dB for rect vs the twin's 1e-6), ghost zone radius growing √10 per 10 dB, taper gain exactly sidelobe difference + ENBW loss, and a 60 dB Hamming zone 6× Hann's despite the lower peak sidelobe. Stylised.
Independent-loss link twin vs a bursty loss chain for repeated map updates: exact residual p·q_g^(r−1), the twin's 5 back-to-back copies leave 81–311× the claimed loss at λ=0.5–0.8, spacing needs 6–36 slots for two copies, and with ≤8 copies the best design is 12–154 slots of latency vs the twin's 4.
Clear-air lidar twin vs fog: detection range W(αr0)/α overstated by exactly e^{αr}, range error is W/(1+W)<1 times the extinction error, a policy sized on median fog is violated 50% of the time (5%-quantile range: 5%, 43.5% slower), and one extinction calibrated on a bright target fails for dark ones in patchy fog. Stylised.
Clear-air or mean-rain-rate radar twin vs intermittent storm-cell attenuation: Jensen gap 1.52× in the rain-rate power law, Lambert-W mean-rate range reached by only 39% of real fields, mean-matching barely helps, a rain ensemble scores Brier 0.038 vs 0.101 clear air. Stylised.
Real test-run length sized in a wrong-pole twin: exact autocorrelated-cost variance, 3.8× too short (coverage 0.69 vs 0.95) or 2.1× too long depending on the real closed-loop pole, and a pilot-run repair that under-sizes half the time.
What a radar twin with unlimited unambiguous velocity over-certifies: exact wrapped-Gaussian bias (−V at μ=V) and MSE with a bias² floor so averaging widens the gap (7.9× → 2.1×10³ at μ=0.8V, n=1→10⁴), safe speed ≈V+sΦ⁻¹(tol/2V), and prior-unwrapping failure 2Φ(−V/√(s²+s_p²)) needing prior error ≤ 0.26V.
Which rungs of a multi-fidelity twin ladder to run: exact nested-estimator variance, a cheaper rung pays iff ρ₂/ρ₁ > 2√r/(1+r) (step correlation, 0.943 for halved cost), using all rungs can be worse than none (1.41× real-only at q=0.9) while the best subset gets 0.83, and a timestep-ladder plant shows 0.156 of real-only variance (0.204 single twin) collapsing to the cheapest twin when disturbance replay is only 90%.
I.i.d.-loss heartbeat twin vs a bursty Gilbert link: a 5-missed-beat watchdog false-trips every 3.4e6 ticks in the twin but every 235–990 on the real link, worst at burst length ≈ m (mean time to trip ≈ e·m/p), and a 1e6-tick target needs m = 16–154 instead of the twin's 5. Stylised.
Gaussian-sensor twin vs a real sensor with outliers under an innovation gate: the twin says the gate costs 8.5% MSE, the real sensor gains 3.0× from it, the worst outlier scale for a gated filter is finite (κ≈4) while ungated error grows as κ², and a gate locks out recovery from a jump for ≈76·D² steps. Stylised.
Rotorcraft altitude twin without ground effect vs real thrust gain 1/(1−(R/4z)²): hover sits 18 mm high at one rotor radius (twin: 0), and a delayed loop with 28% twin headroom goes unstable at 0.54 rotor radii. Stylised.
Linear photon-counter twin of a SPAD lidar vs dead time: half the flux reported at nτ=1, a paralyzable-detector ambiguity (one reading, two fluxes, 12.7× apart at mτ=0.2), first-photon range bias −N/(2√π)σ saturating near −2σ (−22.6 cm at N=10, σ=1 ns) that does not average out, and a Coates correction that removes it. Stylised.
Single-ray lidar twin vs a finite beam with merged pulses at a depth edge: ghost-range band exactly 2Φ⁻¹(1−ε/D) beam widths (2.56 at ε/D=0.1, none at ε≥D/2), shifts and narrows for unequal brightness, matches a scan simulation to 0.3%, and a 3-of-5 persistence filter still passes 80–99% of ghosts.
FMCW range–Doppler coupling: a twin that reads true range misses a bias of f_D T cells (0.6–4.8 at 30 m/s), signal-level check ≤1e-4 cells, wrapped-Doppler compensation is worse than none on half of the over-range speeds, and a ±60° stationary scene leaves 0.71κv position bias plus 0.46κv distortion.
Scan matching in a corridor: along-track information is exactly zero without door frames, 1.6–6× a room's along-track sd with them; a filter fed the room twin's covariance has NEES 432–1535 over a blind span, and the exact covariance holds only inside a ~0.2 m basin. Stylised.
Gaussian-sensor twin vs outliers for a bootstrap particle filter: exact ESS fraction c₀e^{−ay²}, the mean ESS barely moves (0.671 vs 0.645) while P(ESS<1%) rises 120× (2.5e-4 → 3.1e-2), a twin-sized N=528 fails 4.4% of real steps, and posterior-mean error is 45–421× the twin's.
Point/circle/calibrated-inflation footprint twin vs a rectangular robot with heading error in a narrow gap: exact pass probability 2Φ(θ*/σ)−1, circle twins are step functions, a 95%-calibrated inflation is 0.17 m too small at 3× the heading error, 10-gap missions succeed 0.60 where the twin says 1.
RANSAC iteration budget from a fixed-inlier-fraction twin (17 for 99%) vs scenes with beta-binomial inlier counts: exact failure 1.3–30% at that budget, 99% needs 19–458 iterations or is unreachable for κ≤2; stylised, line fitting only.
Lidar twin with independent per-beam visibility vs a Poisson occluder field: beams closer than an occluder diameter share occluders, exact blind probability by inclusion–exclusion over union lengths, 8 beams at 25 cm blind 0.0815 vs the twin's 0.0039 (20.9×), the twin is exact once spacing ≥ 2ρ, an occluder-field ensemble matches. Stylised.
Battery twin with no internal resistance vs a real sagging cell: endurance exactly (1+√(1−u))/2 of the twin's (0.5 at the fold), 9–94% of charge stranded at the voltage cutoff, a burst of 0.5 fails below 51% charge where the twin's floor is 0 (a flat 20% reserve covers only a third of the full-charge limit), and a constant-derate refit errs +12% to +473% off its fit power. Stylised.
How many real trajectories does a classifier two-sample test need to reject a wrong digital twin? Stylised pendulum: for a 20% Coulomb error a paired error test has power 0.98 at 100 trajectories vs 0.25 for the C2ST (which needs ~200), but for a 10% error the paired test stalls at 0.09–0.20 up to 800 while the C2ST reaches 1.00 at 400, and for same-variance noise-shape error the paired test has power ≤0.07 at every size. Null calibration approximate (60 replicates). Preliminary, simulated only.
Was the paired twin test weak, or was its statistic? Stylised pendulum, Student-t noise: the mean squared residual has power ~0.1 at a 10% Coulomb error up to n = 400, while median, trimmed, absolute and Huber statistics reach 0.94–1.00 from n = 50; Gaussian noise barely cares.
Which robust paired test still catches a wrong digital twin when noise has infinite variance or whole runs go bad? Stylised pendulum, 10% Coulomb error: median and trimmed residuals reach power 1.00 under Student-t(2) cells but only 0.17–0.40 under bad runs, where a per-run median reaches 0.89–1.00; no statistic wins both.
Which paired test of a digital twin survives both heavy-tailed cells and whole bad runs? Stylised pendulum, 10% Coulomb error: a two-level statistic (trimmed mean of squared residuals within each run, then trimmed mean across runs) has power 0.99–1.00 at n = 50 under t(2) cells, bad runs at 0.86 and both at once, where the earlier single-level statistics each fail one case. Costs power under Gaussian noise (0.84 against 0.91).
Which significance rule gives a classifier two-sample test the right false-rejection rate on a digital twin? Stylised pendulum: cross-validated rules falsely reject 0.06 to 0.13 at a nominal 0.05, a holdout rank-sum test holds 0.04 to 0.06 at roughly twice the data cost. Preliminary, simulated only.
Does a permutation test on the cross-validated statistic keep its size and beat the holdout rule's power on a digital twin? Stylised pendulum: null rates 0.040 and 0.020, power 0.367 vs 0.183 for holdout at n=200 (Coulomb -10%).
A controller that inverts a linear-thrust twin meets a quadratic thrust curve: realised acceleration is a+a²/(4g), so climbs overshoot more (0.046→0.095) and descents less, and steps below p≈0.5 hardly notice.
Exact square-root thrust inverse vs the linear one on a quadratic-thrust vehicle: up/down overshoot gap 3.00→0.09 points with the right model, but only 3.67→1.65 when the thrust exponent is misidentified (2.5 vs 2).
How much does a wrong process-noise guess cost a Kalman filter? Exact scalar steady state: under-guessing q by ×100 costs ×7.4 MSE, over-guessing by ×100 only ×1.6 (bounded by r), and the under-guessing filter reports 5× too-small error bars. Stylised.
Do low-discrepancy scenarios beat iid domain randomisation for evaluating a policy in a twin? Latin hypercubes only cut MSE 1.6–12× (rate stays n^-0.5); shifted Halton changes the rate for smooth returns (149× lower MSE at d=2) and keeps 4–24× on a success-rate jump, shrinking with d; the R_d lattice is erratic at d=5; 95% intervals from 8 randomisations cover 94–97%. Stylised.
Why does the R_d low-discrepancy lattice lose its edge at d=5 when scoring a twin policy? Not a seed fluke (exponent −0.45 ± 0.01 over six seeds) and not a smooth dimension effect (a dip between d=4 and d=6); a √p generator gets −0.66 at d=5. A simple resonance score does not explain it. Stylised.
How long does a float32 twin of a chaotic system shadow the float64 one, and do its statistics survive? Lorenz and Rössler: float32 departs from float64 after a median 12.3 and 164 time units, like a float64 start error of about 5×10⁻⁶ (100× the float32 roundoff), but the Lyapunov exponent and time-averaged statistics agree within sampling error (stylised).
Does a float32 simulation of a bouncing, chaotic system lose its statistics? Sinai billiard: float32 leaves the float64 trajectory after a median 21 collisions, like a float64 start error of about one unit roundoff, and changes the event order one collision later, but the mean free path and circle-hit share agree with float64 and with Cauchy's exact value (stylised).
Audit of how many research READMEs flag a citation as unchecked: 94 of 550 (17.1%), with Dawid and Skene (1979), Zhang et al. (2019), Horowitz (2014) and Horvitz (1999) the most repeated; counts admissions only, nothing verified.
How much noisy scoring costs the secretary problem: with n = 50 the best cutoff stays at 16–17 (19 noiseless) while P(best) falls from 0.373 to 0.145 at noise 1; cutoff rules only, simulation.
How many simulator rollouts a sequential test saves when certifying a failure rate: exact dynamic programming shows Wald's SPRT uses about half the rollouts of the best fixed test at either hypothesis (79/113 vs 181 for 1% vs 5%), and 6–17% fewer at its worst point in between.
How long can a sequential rollout test run, and what does capping it cost? Exact: the SPRT's 99th percentile is 309 rollouts against a 79 mean (1% vs 5%; fixed test 181), 28% of runs exceed the fixed size at the midpoint rate; capping at the fixed size adds 34–38% to the error, a cap of 1.5 times it keeps the error at 0.053 to 0.057 for a mean within 2% of uncapped.
With noisy scores, a rule that must beat the earlier best by a margin raises P(pick the true best) from 0.233 to 0.244 at noise 0.5 and 0.143 to 0.149 at noise 1 (n = 50, fresh-trial test); no gain at noise 2; simulation.
Does a sampled-data loop tuned on a fixed-period twin survive random sampling intervals? Uniform jitter up to ±100% never destabilises it, but missed samples do: almost-surely stable up to miss probability 0.556, mean-square stable only to 0.270 (0.05 for a deadbeat tuning); at 0.4 all 2000 simulated runs converge. Stylised scalar model.
Does retuning the gain on the sampling-interval law, instead of the fixed-period twin, remove the missed-sample penalty? Yes for this plant: the mean-square-optimal gain is stable at every miss probability (worst E g² 0.478 vs a twin-gain limit of 0.270), at the price of a slower nominal loop; a gain designed for q = 0.3 stays stable at every true q. Stylised scalar model.
Research programme (proposal stage): per-quantity error budget for a Froude-scaled cargo aircraft model, with a stdlib scaling calculator; first-order result: at 1:10 the model needs 17 to 35% more power than Froude scaling predicts
Does a physics-shaped twin of a real buck converter beat plain ARX? Only partly: all models sit at 0.5 to 0.9 V free-run error against a 0.06 V quantisation floor, and the winner flips with which half of the 20 ms record is fitted. One 20 ms record; natural frequency fitted, no component values.
Exact: a fixed-step twin under-reports a PD loop's delay margin by 18.6% at dt = 0.1 s and 1.0% at 5 ms, because the largest stable delay is the largest n with (n + 1/2) dt below the true margin (25 of 25 cases)
How wrong is a simulator's pendulum period at its default timestep? Exact elliptic-integral period against Euler, semi-implicit Euler, Verlet and RK4: Euler fails (14% period error at 2 ms), the symplectic pair is 0.75 ppm, and releasing from rest hides the symplectic error.
Which 95% upper bound on a failure rate really covers 95% at rollout sample sizes: exact coverage shows only Clopper-Pearson never undercovers (min 0.950), Wilson dips to 0.93, Jeffreys to 0.85 and Wald to 0.06–0.75; zero-failure certification of p ≤ 1% takes 299 rollouts (CP), 268 (Wilson) or 191 (Jeffreys).
How many fixed steps per orbit does a twin need before an eccentric orbit stops drifting? Against the exact Kepler solution RK4 needs 64 to 4096 steps per orbit (e = 0 to 0.9), the symplectic pair 8 to 16 times more, and at e = 0.9 every fixed step fails.
How long does a digital twin of a chaotic system stay accurate? On Lorenz-63 each e-fold of smaller state error buys 1.12 time units (1/lambda = 1.11); a parameter error buys 0.85. Mean over 40 starts, one tolerance.
How many missed samples can a PD loop tuned on a fixed-period twin survive? With samples lost independently and the last command held, a double-integrator loop with twin poles at 0.5 is mean-square stable only up to a 29% loss rate but almost surely stable up to 61%; a deadbeat twin tolerates 7% in mean square.
On a linearised pendulum (L = 0.5 m) a fixed twin-tuned gain survives any miss probability with slow poles unless the plant is very unstable per sample (limit q = 0.21 at ωh₀ = 1.4), a deadbeat tuning fails by q = 0.03 to 0.10, and a gain recomputed from the actual interval was stable at every q in all 15 cases. Linear, noise-free, simulated.
How many solver iterations does a physics twin need to hold a stack of boxes still? A projected Gauss-Seidel solver at 60 Hz needs 16 for 4 boxes, about 128 for 6 and over 2048 for 16 or more, and extra iterations do not reliably help.
Exact: a twin that fails 10% less often than reality lifts the chance of certifying a 5%-failure policy from 0.049 to 0.087 (fixed test, 1% vs 5%), 20% less often to 0.147, and guarding against a 1.5x optimism costs 2.2 times the rollouts
Follow-up to free-sprtcap: re-tuning a capped SPRT's boundaries and final cut so both errors stay at or below 5% exactly costs, for 1% vs 5% (fixed test 181 rollouts), a mean of 107 rollouts at a cap equal to the fixed size and 90 at twice it, against 90 to 95 for the plain capped test that overshoots the error; the fixed test needs 181.
Follow-up to free-sprtopt: an exact linear programme gives the capped certification test with the smallest worst-case mean over failure rates between p1 and p0; for 1% vs 5% at a cap of 362 it needs 123.8 rollouts at worst against 131.0 for the average-optimal test and 181 for the fixed test, at the price of 3 to 6% more rollouts at the two design rates.
Follow-up to free-sprtcut: backward induction gives the optimal capped test, 98.9 rollouts on average for 1% vs 5% at a cap of 181 (proved within 0.2% by a dual bound), against 107.3 for the grid-tuned SPRT and 181 for the fixed test; the tuned SPRT is 3 to 9% above the optimum at every cap tried.
Is the overflow twin's lead over black-box models on a real two-tank rig statistically real? A 0.13 V RMSE gap over ARX 4/4 with a block-bootstrap 95% interval of 0.06 to 0.20 V; the iid bootstrap is about three times too narrow. Test-trace sampling only, not fit variance.
Does the overflow twin's lead over ARX survive refitting on a real two-tank rig? A 0.13 V gap in 100% of refits with 87.5% of the training data, but 0.07 V and 84 to 90% of refits with 50 to 75%. Overlapping windows, fixed optimiser start.
Does a physics digital twin beat black-box models on a real two-tank rig? An 8-parameter overflow twin gets 0.53 V test RMSE against 0.66 V for the best black box (9-parameter ARX); quadratic NARX models diverge in free run. One rig, one split, no confidence interval.
A 3D-printable 22-DOF bimanual mobile manipulator (two 7-DOF arms with geared elbows and parallel grippers, head, lift, omni base) on one $15 servo, $627–948 in parts, with a MuJoCo twin generated from the same parameters as the CAD: reach and pick policies trained on the exact twin ignore servo, friction and mass errors but fail at one 40 ms step of latency (reach 99→29%, pick 91→41%); randomisation fixes reaching almost for free but costs picking 14 points; an interference sweep over the printed solids caught an elbow range the twin allowed but the parts could not reach. Simulated only, not yet built.
Research programme (milestones 3 to 6 logged): valid, bias-agnostic sim-to-real evaluation of robot policies, consolidating about 130 twin projects into one question, with 13 checked references, hypotheses H1 to H6 and CoRL as the target venue
Open-source hardware design flows (Yosys, Icarus, Verilator, OpenROAD) and the loops that put language models in them. Topic page →
Reproducible open RTL flow (Yosys, Icarus, Verilator): gate count and depth for adders, a multiplier and a FIFO, SAT equivalence of two adders plus a broken-adder control. Gate counts, not silicon.
What lint, random simulation and a Yosys equivalence proof each catch, on 12 small RTL tasks (companion to chip-rtl-loop); mutation probe shows 30 of 389 rejected bugs are caught only by the formal proof. Session-written attempts, not an LLM benchmark.
Lint, simulation and formal-equivalence feedback for Verilog repair on nine small tasks; 6/9 pass at round 0 and 9/9 after one round, with the session as proposer (anecdotal, not an LLM benchmark).
No-model mutation-repair baseline for a scripted Verilog checker (compile, lint, simulation, SAT miter) on ten small tasks: 9/20 one-fault cases repaired in 60 evaluations; the session agent passed all ten first try, so the feedback loop is unmeasured. Preliminary.
Equivalence-gated area/depth rewrites of a 16-bit adder and 6x6 multiplier against a no-model parameter sweep; best adder 0.85x the reference cells×depth, tied by the sweep, no multiplier gain (stylised, gate counts).
How generic-gate cells and depth scale with bit width for seven arithmetic blocks: adder, comparator and mux are near-linear, the multiplier quadratic (exponent 2.19), and adder depth grows ~2×W (stylised, generic gates).
Fixed-weight multipliers for all 255 8-bit constants: Yosys's x * K tracks binary shift-add (Pearson 0.97 with set bits), and a canonical-signed-digit form has 33% fewer generic-gate cells at similar depth (every form proved equivalent).
A bank of fixed-weight multipliers sharing sub-sums (multiple-constant multiplication): 9% fewer generic-gate cells than per-constant signed-digit shift-add at 2 constants and about 20% fewer at 8 and 16 (43% fewer than Yosys's *), every form proved equivalent; random constants, not trained weights.
How many gates an exact 4-input rewriter could still remove from real Yosys/ABC netlists: none in 28 of 30 runs (1 gate in two), even where the default script beats plain mapping by 25 to 42%, so the flow's gains are not local.
How far above the SAT-proven minimum gate count Yosys/ABC lands on 4-input logic: the default flow is exactly optimal on only 34% of sampled functions (mean 1.19 gates above, max 4), and a heavier script is worse.
Sweeps five ABC scripts over five adder and eight multiplier structures (all proved equivalent): the script moves cells×depth by up to 1.75× for one adder, while all eight multiplier structures score identically (stylised, generic-gate).
Whether equivalent Verilog that differs only in wire names, statement order or the order of added operands synthesises to the same size: names and statement order never change cells×depth, operand order does for one carry-select adder (up to 1.43×, a 17% better result than the earlier sweep's best; stylised).
Tests whether carry-select blocks share a+b independently under mixed per-chain operand orders: the set of sharing blocks predicts Yosys's adder count in 400 of 400 random variants and fixes the cells x depth score (8 sets, one score each per ABC script); the cost is not additive across blocks (stylised, Yosys 0.33).
Finds the Yosys pass behind chip-abc-order's operand-order effect: opt_merge shares a+b between the two carry-select sums only when both are written with a and b first (4 of 36 operand orders); removing it widens the spread (up to 3.2×), so it was hiding variation. One adder, stylised.
Tests whether letting Yosys share a common a + b shrinks adders: fewer cells in 54 of 55 design/script pairs but often deeper; stylised, Yosys 0.33.
Writing the shared a + b sum of a carry-select adder by hand (explicitly, or as an incrementer) gives the same netlist Yosys already finds; attaching the constant to b first defeats the sharing and is 17-22% smaller under ABC's optimising scripts (stylised, Yosys 0.33).
Re-scores the chip-ppa-loop rewrites and sweep under five ABC scripts with every mapped netlist proved equivalent: the adder rewrite gain survives (0.80–0.86× the reference per script) but the multiplier's whole gain is the script (stylised, generic-gate).
Equivalence-gated rewrites of 16-bit popcount, 16-bit leading-zero count and 8-bit |a−b| against a no-model sweep: popcount 0.98×, |a−b| 0.86×, but on leading-zero count the sweep (0.56×) beats the session-written rewrites (0.80×) in 168 of 200 equal-budget draws (stylised, gate counts).
Re-scores chip-ppa-logic's popcount, leading-zero-count and |a−b| candidates under five ABC scripts with every mapped netlist proved equivalent: the clz16 sweep-versus-rewrite verdict flips with the script (best 0.35× the reference); stylised, generic gates.
A fused 4×4 multiply-accumulate: no written rewrite beats a*b+c under the default or three of five ABC scripts, but carry-save forms win by up to 9% cells×depth under dch and resyn2 (stylised, generic-gate).
The chip-ppa-mac carry-save MAC rewrites mapped to SKY130 HD cells: the plain a*b+c under its best script is the overall best, the generic-gate score ranks candidates only weakly like cell areaxdelay (Spearman 0.20; stylised, ABC delay estimate).
An exhaustive 800-point table of SKY130 areaxdelay over ABC pass sequences for the MAC (optimum 11% below the best earlier script; needle-like landscape), with random search, hill climbing and session-written proposals compared at equal budget (stylised, preliminary).
Parameterised MAC-lane accelerator for an 8-8-4 quantised MLP, bit- and cycle-exact against NumPy in Icarus; lanes x bit-width sweep puts the cells-times-cycles minimum at 4 lanes (stylised, generic-gate counts).
Synthesis-only area and delay versus placed-and-routed OpenROAD numbers on SKY130 for 13 small designs (stylised, global-route estimates).
R x C output-stationary systolic MLP engine, bit- and cycle-exact against NumPy; at matched MACs it loses to chip-accel's MAC lanes on cells-times-cycles (about 1.6x to 1.8x) but wins on latency (negative, stylised, generic-gate counts).
Batch-size sweep of the systolic MLP engine (R = 4, 8, 16): the array's cells-times-cycles disadvantage against chip-accel's MAC lanes widens from 1.6x to 2.9x because its area grows with the batch (negative, stylised, generic-gate counts).
Small reused systolic arrays (R = 1, 2, 4 rows) against chip-accel's MAC lanes: even the best, 1x4, has 1.35x the cells-times-cycles per vector (65702 vs 48546) at fan-in 8 (negative, stylised, generic-gate counts).
Fan-in sweep (F = 8, 16, 32) of small systolic arrays against chip-accel's MAC lanes: the best array costs 1.36x, 1.25x and 1.26x the cells-times-cycles per vector of the best MAC engine, so the gap narrows but does not close (negative, stylised, generic-gate counts).
Extends the fan-in sweep past its edges (C = 16, P = 32): the optima move inward and the best array still costs 1.25x (F = 16) and 1.20x (F = 32) the cells-times-cycles per vector of the best MAC engine (negative, stylised, generic-gate counts).
Builds and RTL-checks every MAC-lane count P = 1 to 20 on the F-16-4 network (F = 16, 32): the best P is 8 and 16, no non-power-of-two wins, and P above 16 only adds cells (stylised, generic-gate counts).
Widens the hidden layer to 16 (F = 16, 32) and lets the MAC engine reach P = 16: the best MAC engine still beats the best systolic array, by 1.30x and 1.27x in cells-times-cycles per vector, and at F = 32 its best lane count is again the largest tried (negative, stylised, generic-gate counts).
Extends the hidden-16 comparison to MAC lanes up to P = 32 and arrays up to 4x8 with every design simulated: the best MAC engine still wins, by 1.30x and 1.28x in cells-times-cycles per vector; P = 32 adds no cycles over P = 16 (negative, stylised, generic-gate counts).
Re-scores chip-systolic-p32's 20 designs under five ABC scripts: the best MAC engine beats the best systolic array in all ten F x script cases, by 1.28x to 1.60x (negative for arrays, stylised, generic-gate counts).
Re-synthesises the 16- and 32-lane MAC engines (same cycles) with three seeds and three Yosys flows: the sign of the cell-count gap depends on the flow, with swings of 1-10%, so chip-systolic-p32's 0.7% ranking is not reliable (artefact-sensitive, stylised, generic-gate counts).
Counts cells of the 16- and 32-lane MAC engines after the word-level, bit-level and abc stages: the 32-lane engine is bigger at the word level, about 500 cells smaller after techmap, so the chip-macp32cells gap is set before abc (localised, mechanism unexplained, stylised).
Runs the Yosys fine passes one at a time on the 16- and 32-lane MAC engines: the P = 32 versus P = 16 sign flips (+2,100 to about -120 cells) at the first opt -fast after techmap, before any abc, and chip-p32netlist's pre-abc label is corrected (Yosys 0.33's -run :abc includes abc -fast). Stylised.
Weight and activation bit-width sweep of a 64-16-10 quantised MLP on the scikit-learn digits data (5 splits), with the MAC lane's gate count from Yosys and its RTL checked against NumPy: 4-bit weights and activations lose about 2 points of accuracy, 5 and 5 about 0.5, below 3 bits it collapses.
Giving each neuron of the digits MLP its own power-of-two weight scale turns the per-channel rescale into one or two shift stages and keeps the lane integer-exact: at W2A4 the MSE-chosen exponents reach 70.5% (against 62% for per-tensor clipping), but at W3A4 they give 87.9%, below clipping's 90.8%.
MSE-optimal weight clipping lifts the 3-bit-weight digits MLP from 81% to 91% test accuracy at the same MAC-lane hardware and integer-exact; per-channel scales and QAT help at 4 bits (95.7% at W4A4, within 1.1 points of float) but QAT fails at 2 bits.
Can general-purpose robot arms make and assemble things, planned and checked in simulation first? Assembly sequences, insertion and cells, with every claim kept to the simulator. Topic page →
Assembly-order planning for a printed gearbox: exact subset DP, collision-only admits 10.6% of orders but support checking leaves 0.077%, the collision-only optimum is infeasible, greedy disassembly needs 4 direction changes vs 1 optimal. Stylised.
MuJoCo settle tests of all 2,048 partial gearbox assemblies vs the quasi-static support rule: 95.6% agreement, 81 mutual-support false accepts and 10 bore-capture false rejects, valid-order count unchanged at 30,760. Stylised.
Peg-in-hole search policies tuned by CEM in MuJoCo at three fidelity levels or with domain randomisation: tuned on the simplest level 0.91 success there but 0.53 / 0.26 on a stiffer-contact / held-out level; training on the stiffer level or with randomisation gives 0.43–0.46 held-out and cannot be ranked with 5 seeds. Stylised, sim-to-sim.
Session-written pick-and-place programs checked in a kinematic SCARA twin at three fidelities against a held-out reference: of 69 reference-failing injected-bug mutants the levels reject 38, 46 and 60 with no false alarms; misses are unmodelled effects (stylised).
Discrete-event twin of an arm, printers and an inspection station: printers have the highest utilisation at every size, yet at 6 printers an extra arm saves 10.9 min vs 2.3 for an extra inspection station; dispatch rules trade makespan for flow time; a mean-value twin is optimistic. Stylised, illustrative parameters.
Discrete-event twin of an arm, 3D printers and an inspection station: a utilisation bound names the bottleneck (printers to 10, the arm from 12, ~12.7 good parts/h) and the simulation sits 10–11% below it near the switch; a 25% faster arm lifts 11.34 to 12.68 parts/h at 12 printers, a second inspector nothing (stylised).
Exact mean value analysis of the arm, printers and inspection network against a discrete-event twin: a few per cent off for exponential times, up to 11% low for less variable ones, better than the utilisation bound in most real-semantics rows, and it overshoots saturation at high work in process. Stylised.
Coefficient-of-variation sweep and a measured printer stall share for the arm-printer-inspection queueing model: MVA's error crosses zero near cv 1 while the utilisation bound stays high, and held-printer capacity times (1 − stall) reproduces the saturated rate at 4 and 8 printers. Stylised.
Is a print-failure camera worth it in a robot-arm printer cell? Blind printing against abort-on-failure: +6 to 10% good parts per hour at 2 to 10 printers, none once the arm limits the cell; break-even false-stop rate. Stylised.
Where should a print-failure detector's alarm threshold go in a robot-arm printer cell? A look every 2 min makes a z = 2 threshold 19 to 23% worse than blind printing; the best z is 3 to 3.5, worth +6% (d' = 2) to +11% (d' = 4). Stylised.
Where does the flow-equivalent-server decomposition of a robot-printer cell err as the inspector speed varies? Error is 0 for fast and slow inspectors but peaks at −2% to −5% just below the knee where inspector and subsystem rates match, ten times the earlier 0.3% mean. Stylised.
Can a flow-equivalent-server decomposition predict a robot-printer cell without enumerating its states? Mean error 0.3% (max 1.6%) against the exact Markov chain in 42 settings, where plain MVA is off by up to 20%. Stylised.
Is the error of queueing analysis of a robot-printer cell from print-time variability or from structure? An exact Markov chain says structure: cv 1 to 0.33 moves throughput by at most 0.71%, while plain MVA overshoots up to 20% beyond the printer count.
Does adding load and unload time to the printer's demand fix MVA of the robot-printer cell? Mixed: it cuts the error at saturation (2.9% against 8.2%) but raises it elsewhere (7.3% against 3.6%), so overall plain MVA is better (4.7% against 6.2%). Stylised.
Does adding the arm's queueing delay (a fixed point, no fitted parameter) to the held printer's demand fix MVA of the robot-printer cell? No: it underpredicts in all 32 settings and is worse overall (7.9% mean error against 6.2% for held-demand and 4.7% for plain MVA). Negative result. Stylised.
Can a blocking-aware correction to MVA predict the held-printer robot cell across loads? A fitted stall helps only at saturation (1.4% error) and worsens other loads (8.5%); keeping latency apart from capacity gives 3.6% against plain MVA's 4.7% on the design grid, but only ties plain MVA (3.4% against 3.5%) on a held-out job mix. Stylised.
Can a parallel-jaw arm assemble its own toy gripper? A complete order exists only once the jaw opens to the widest part (30 mm); a top-down-only arm accepts 120 of 720 orderings against 384 with sideways moves; pad thickness changes nothing (negative). Stylised boxes.
Can a printed gripper assemble its own next generation? With fixed-size jaw pads a gripper builds a copy only at scale ≥ pad thickness in mm (4 mm pads: scale 4); a stroke cap of S mm needs 30·pad ≤ S; seeds of 130 and 140 mm sustain a chain, 60 and 100 mm decay. Largely algebraic given an assumed opening; stylised.
How long an arm does it take to assemble its own toy gripper? A planar two-link arm needs 60–140 mm links as the tray moves 40–400 mm away, and a 90° elbow limit more than doubles it (stylised).
Does the assembly order change the arm needed to build its own gripper? Across all 384 valid orders the shortest arm is identical in every setting tried (negative result, stylised).
Can friction hold each printed part of the toy gripper? The simulated minimum jaw force matches the m·g/(2μ) bound to within 5% over 33 cases and is at most 0.1 N, so the jaw opening, not friction, is the constraint (stylised).
Does arm torque or jaw friction limit how fast an arm carries a printed part? With 0.12 m links and 5 N m the carries take 0.06–0.10 s and the cover needs 1.25 N per jaw (21× static); grip binds below about 0.5 N (stylised, bound extrapolated beyond 40 m/s²).
How much carry time does a time-optimal move save over min-jerk, and what does it cost the jaws? On the robofab-armaccel arm the six-part total falls by 21 to 29% while the jaw-force bound rises 1.2 to 2.4 times (stylised, assumed parameters).
How fast can an arm carry a printed part when the jaw force is capped as well as the joint torque? On the robofab-armbang arm the time-optimal move still beats min-jerk by 17 to 43% under caps of 1.25 to 10 times the static hold force, and a tight cap makes the torque limit irrelevant (stylised, assumed parameters).
Does a joint-speed limit erase the time-optimal carry's advantage over min-jerk? On the robofab-jawcap arm it grows it: 28 to 46% shorter under speed limits of 6 to 1 rad/s, tending to the 47% set by the min-jerk profile shape (stylised, assumed parameters).
Is the time-optimal carry's speed-limited advantage just the min-jerk shape? Against a tuned trapezoidal-velocity move it is only 0.4 to 2.9% at speed limits of 2 and 1 rad/s (46% over min-jerk), and 8.7 to 22.5% with no speed limit (stylised, assumed parameters).
Does rounding the trapezoid's corners (a jerk-limited S-curve) change the time-optimal carry's edge? An S-curve is never faster than the trapezoid and costs 0.0 to 2.0% (half-jerk) or 0.0 to 7.0% (full-jerk) at speed limits of 2 and 1 rad/s, but 1.4 to 33.7% with no speed limit (stylised, assumed parameters).
Checks robofab-scurve on a finer ramp grid: sampling a 0.2% ramp is needed or the trapezoid wrongly beats the time-optimal solver; with it the time-optimal edge at 2 and 1 rad/s is −0.3 to +0.9%, below the solver's own ~0.5% node-count error (stylised, negative on the old figure).
Re-solves the time-optimal carry at 400, 1600 and 6400 nodes in all 12 speed-limited rows of robofab-scurvefine: once converged the edge over a tuned trapezoid is positive everywhere, +0.1 to +0.9% (stylised).
Golden-section tuning of the trapezoid's ramp fraction shrinks the time-optimal carry's edge to +0.05 to +0.28% (still positive in all 12 rows; stylised).
Repeats the robofab-motorcurve motor-line rows with the time-optimal solver at 400, 1600 and 6400 nodes: the edge over the tuned trapezoid moves by at most 0.28 points from 1600 to 6400 (the 0.08 m, k = 2, w0 = 4 row rises from 4.98 to 5.26%), and the missing cover profile was a node-count limit. Stylised.
Re-solves the nine torque- and jaw-bound robofab-torquebound rows with a motor torque-speed line (no-load speed 4 to 20 rad/s): the time-optimal carry stays faster than the tuned trapezoid in all 45 cells, but its edge ranges 3.5 to 28.6% (9.0 to 22.9% under a constant limit), shrinking where a jaw cap binds and growing where only torque does. Stylised.
Re-checks the nine torque- and jaw-bound robofab-torquebound rows with a dense trapezoid peak check (10,000 whole-move samples, 1,000 per ramp, both sides of the acceleration corners): trapezoid totals move by under 0.16% and the time-optimal edge stays 9.5 to 23.0%, so the large edge does not rest on unseen trapezoid peaks. Stylised.
Re-checks the 108 trapezoid and time-optimal carry profiles of the robofab-torquebound rows against MuJoCo inverse dynamics: the hand-written two-link torques agree to 1.8e-5 N m, peaks are within 0.73% of the 5 N m limit (stylised, joint torques only).
Re-checks the torque- and jaw-bound rows of robofab-scurve (no speed limit) with a converged solver and denser trapezoid ramp sampling: the time-optimal carry is still 9.4 to 23.0% faster than the tuned trapezoid in all 9 rows, and the edge is stable to solver node count (under 0.1%) and rises by at most 0.4 points with denser sampling. Stylised.
Re-solves the time-optimal carry of robofab-scurvefine at 400 to 25600 nodes in all 12 rows: converged to 0.02% by 6400 nodes, the 400-node answer was up to 0.5% pessimistic, and the converged edge over a ramp-resolved trapezoid is 0.11 to 0.88% in every row; stylised, preliminary.
How hard must the jaws squeeze while the arm moves? Simulated minimum force matches the m·sqrt((g+a)²)/(2μ) bound within 7% over 77 cases and is at most 0.3 N at 40 m/s²; a contact time constant that passes the static test reports slip at any force once the jaws accelerate (stylised).
Does the jaw-force bound still hold at arm accelerations of 100 to 800 m/s²? With fine MuJoCo contact settings the minimum force is 0.89–1.02× the bound over 39 cases; the earlier settings fail above 200 m/s² (stylised, prescribed acceleration, no arm).
How fine must MuJoCo contact settings be for a moving grasp? On all seven toy-gripper parts, solref 0.2 ms and below reproduce the jaw-force bound (0.98–1.04×) at 100–800 m/s²; 0.5 ms fails at 400 and above, and the adequate value falls with acceleration (stylised, upward load only).
Is it solref or the timestep that breaks a moving MuJoCo grasp? On a 24-cell grid only 6 cells hold; a coarse step always fails, a finer step does not rescue a marginal solref, and solref 0.1 ms holds at steps of 0.1 ms and below (stylised).
Does MuJoCo's refsafe clamp break a moving grasp at a coarse timestep? Switching it off changes 7 of 32 grid cells' outcomes (11 hold on, 10 off), 10 runs go unstable, and the non-monotone timestep behaviour survives (stylised).
Does an off-centre centre of mass need a harder grasp? Ball-pad elliptic-cone bound matches MuJoCo within 1.1% (5× force at 20 mm offset); flat-pad MuJoCo lies between an equal-split and a best-split corner-contact bound (stylised).
Does the friction-grasp bound survive lift acceleration and an off-centre centre of mass? Scaled bound matches MuJoCo within 6% over 66 cases; the torque bracket for an off-centre bar is inconclusive and depends on the rotation tolerance (stylised).
Is the off-centre bar result in robofab-liftload a grasp effect or solver creep? The bar creeps at about 3.7 deg/s from 0.3 to 3 N in MuJoCo, with a rate set by contact settings, so the earlier verdict reflects the simulator (stylised).
Does a rate-based "holds" criterion make a MuJoCo grasp verdict independent of solver settings? No: the minimum holding force still varies 33x to 400x or more across contact settings, like a 1 degree tolerance (negative, stylised).
Is any rate threshold settings-robust for a MuJoCo "holds" verdict? Spread falls with the allowed tip speed and is 1.6 only at a loose 20 mm/s (0.5 s, 10 mm); 242.7 to 400 at 2 mm/s or less (stylised, preliminary).
Does the loose 20 mm/s "holds" threshold stay settings-robust at other friction and under lift? It is the only threshold under 5x spread in all six conditions (1.6 to 4.5), every other is at least 20x (stylised, preliminary).
Does a stiffer friction cone make the held-bar result threshold-free? Creep falls about as 1/impratio (3.66 to 0.004 deg/s); from impratio 10 the 1 and 5 degree forces agree within 26%, and MuJoCo needs 0.67 to 1.17 times the old torque bracket's lower bound (stylised).
How much clearance does a printed two-pin cover need to assemble, and how wasteful is worst-case stacking? At position sd 0.10 mm and size sd 0.05 mm, 99% yield needs 0.62 mm diametral clearance and a ±3σ worst-case stack asks for 2.0 mm (stylised, assumed process spreads).
Zero-order milling stability lobes against semi-discretisation and time-domain simulation for a one-mode tool: exact at slotting, but at 10% up-milling the limit is up to 3.3 times too high at some speeds, and in down-milling the zero-order chart predicts no chatter while the tool goes unstable below 0.9 mm; the best spindle speed raises removal rate 5 to 18 times.
Follow-up to infra-sortvalue: an exact dynamic-programming bound on the best possible pick schedule (agreeable deadlines make arrival order optimal) shows highest-value-first dispatch reaches 96.5% of the clairvoyant optimum at 6 items/m and 93.9% at 10, FIFO 94.7% and 89.6%, and that the largest headroom (about 10 to 11%) sits at faster belts and slower arms, not at the loads where pick order helped most. A rolling-horizon rule that re-solves the schedule with a 1 s look ahead recovers most of it: 99.7% of the optimum at 6 items/m and 98.0% in the hardest cells.
Single-robot conveyor pick cell fed with the class mix and object sizes of the 4,784 TACO litter annotations: with a 1 s pick and 1 m of reach, recovery of bottles and cans holds near 0.65 up to 0.5 m/s, falls to 0.48 at 1.0 m/s and is zero from 1.5 m/s (reach/pick-time is a hard limit); detector size threshold and false-call rate move purity and recovery more than the pick-order policy, which changes nothing.
Follow-up to infra-sorting: with TACO's class mix, assumed item values (drink can = 4 plastic bottles) and 0.5 to 1.5 s of arm travel, picking the highest-value item first beats FIFO by only 0.1% at 1 item/m, 2.0% at 6/m and 4.8% at 10/m, and value-per-second picking matches it; belt speed and pick time matter far more than pick order.
An always-on, audio-first assistant: when it should speak, and how fast and cheaply the pipeline runs on a device. Simulation first, no real recordings. Topic page →
CPU voice pipeline (Silero VAD, Whisper tiny.en, Qwen2.5-0.5B, Piper) on synthetic speech: per-stage latency/RTF/memory and a reply-latency budget of 0.9–1.5 s at 200–800 ms endpoint hangover, ~0.7 s of it compute. Server CPU, not a phone.
When an always-on assistant should speak: wake, keyword, threshold and learned policies at equal annoyance, and what breaks when the simulator's room differs from the real one
How much speech-recognition error hurts an always-on assistant's trigger policies at equal annoyance: from word error rate 0 to 0.5 a two-word wake phrase loses 74% of its recall and a transcript-reading threshold 76%, an acoustic-only score about 54%, and the transcript policy falls behind the acoustic one at WER 0.3 to 0.4 if its separation shrinks as (1-WER)^2 (stylised).
When moments of need cluster in time, does a cooldown, boost or back-off help an always-on assistant at equal annoyance: an episode-aware boost gains up to 0.05 recall under strong clustering, a cooldown always loses recall, back-off is a wash; stylised simulation.
What an on-device assistant should keep from a week of simulated transcripts: BM25 retrieval, extractive summaries and byte-limited retention policies (stylised)
Testable Kotlin core of an always-on listening service (re-framing, energy VAD, utterance segmenter, headset-drop policy; 7 tests pass under a shim) plus an unbuilt Android foreground-service sketch; no SDK, no device numbers
When a glanceable display beats speech for an always-on assistant: a stylised utility model over noise, company, free eyes and message length, with sensitivity and twin-gap checks
Urgency classes and a chime-plus-glance mode added to the glance-vs-speech utility model for an always-on assistant: a stylised model with sensitivity and twin-gap checks
How much reply latency starting the ASR/LLM/TTS chain during the end-of-speech hangover hides, from the measured ambient-pipeline stage times and an assumed within-turn pause model (hold-until-endpoint vs eager; extra runs per turn)
Can a sentence-completeness cue let an always-on assistant stop waiting so long before it replies: a stylised two-hangover endpointer cuts the mean wait from 913 to 574 ms at a 10% cut-off budget if no pause sits at a complete point, but only to 837 ms if half do; cue and pauses assumed.
How many repeated earbud tones before a glance are worth their annoyance, by urgency, tone gap and masking, in the ambient-urgency utility model (stylised)
How accurate an urgency label must be before an always-on assistant should act on it: naive, Bayesian and label-ignoring policies in the ambient-urgency utility model (stylised)
How many audited messages an assistant needs to estimate a noisy urgency label's confusion matrix and prior well enough to act on it: about 50 at moderate accuracy, with smoothing helping at tiny audit sets (stylised)
What a noisy human auditor does to an assistant that learns its urgency label's reliability from audits: taking audit labels as truth biases the estimate and loses 8% to 69% of the label's gain at a 0.9 to 0.7 auditor, and correcting for a known auditor accuracy recovers it (stylised)
How many gold-labelled audits replace noisy ones when the auditor's accuracy is unknown: 25 gold audits match 1000 noisy ones read as truth, and a joint EM using 10 gold plus 200 noisy audits nearly reaches the true-parameter policy (stylised)
How to split a fixed audit budget between gold and noisy audits when gold costs 3 to 30 times more: all-noisy is worst or near-worst in all 12 cells, 25% on gold with a joint EM fit is within 0.0009 of the best, and all-gold loses when gold is expensive (stylised)
Can the assistant learn its urgency label's reliability from two noisy auditors with no accuracy known (Dawid-Skene), and what does a wrong assumed auditor accuracy cost: over-trusting the auditor loses 31% of a 0.9 label's gain, and Dawid-Skene reaches within 0.0005 of the oracle at n = 1000 (stylised)
What does Dawid-Skene do when the two auditors share their errors: it over-trusts them (auditor accuracy read as 0.909 for a true 0.8 at half shared) and loses part of its edge over trusting one auditor, falling to equal it when the second auditor is a copy, never below it (stylised)
What if the auditors only share errors on hard messages: Dawid-Skene's cost is much smaller than with copying (policy utility 0.4060 vs 0.4066 at 30% hard messages), reaching the naive estimator only in an extreme cell, and a hardness-aware EM recovers the classifier but cannot identify the hard share (stylised)
Does a third auditor identify the hard-message share: yes at the population level (P(hard) 0.300 from informed starts), only loosely at n=1000 (sd 0.07), and in the extreme cell plain Dawid-Skene with three auditors falls below the naive estimator (0.3912 vs 0.3992) while the hardness-aware EM does not (stylised)
Does a likelihood-ranked multi-start make hardness-aware Dawid-Skene robust to a poor start: at the population level yes (P(hard) 0.300, vs 0.500 and a lower likelihood from a poor single start), at finite n it matches one informed start, and where hardness is absent the hard share is not identified (stylised)
How many starts does a likelihood-ranked multi-start need, and are grid starts better than random ones: one start is nearly enough with strong hardness or n = 1000, 4 starts reach the best optimum in most cells, more help only in the weak-hardness and null cells, and policy utility barely moves (stylised)
Can a likelihood-ratio test tell no hard messages from some: chi-square cutoffs reject 35-72% of null data sets, a parametric bootstrap holds its level and detects h = 0.3 at n = 1000 but not h = 0.1 (stylised).
Does the bootstrap likelihood-ratio test of no hard messages hold its level: 200 null draws per n give rejection 0.040-0.055 at nominal 0.05, all intervals containing 0.05 (stylised).
Does the no-hard-messages bootstrap test keep its level when the three auditors differ in accuracy: 100 h = 0 draws per cell give rejection 0.00-0.10 at nominal 0.05, no inflation seen (stylised).
Can an always-on assistant learn when to speak from accept/dismiss feedback alone: greedy, epsilon-greedy and Thompson online policies vs an offline oracle, mostly negative (stylised)
Does inverse-propensity weighting fix an assistant learning from its own accept/dismiss feedback: mostly negative, exploration cost dominates (stylised)
Does selection bias hurt an assistant learning only from windows where it spoke: yes, a lot in this world; a full-information fit reaches the oracle, weighting recovers part (stylised)
Is the self-selected-feedback gap bias or label volume: mostly bias (a random sample of equal size nearly reaches the oracle); clipped weights help only with an informed prior (stylised)
Does a doubly robust estimator beat IPS on an assistant's self-selected feedback: no, a stylised negative result; its pseudo-labels carry 1/ε residuals and are worse than the biased fit except with an informed prior.
Does capping the inverse-propensity correction rescue doubly robust learning from an assistant's own feedback: with an informed prior yes (the collapse at ε = 0.002 goes from 0.26 to about 12 utility/h), with an uninformed prior no; stylised, simulated only.
Does fitting the doubly robust outcome model out-of-sample (2-fold cross-fitting) help the capped correction: no, a negative result; differences are within seed noise or worse, and the unclipped collapse at ε = 0.002 persists (1.53 vs 0.26 utility/h); stylised, simulated only.
Can the capped doubly robust cap be chosen by 4-fold IPS validation on the log: with an informed prior it matches the best fixed cap within seed noise, with an uninformed prior it does not rescue learning; stylised, simulated only.
A doubly robust validation score does not pick the DR cap better than IPS with the same 4 folds (equal with an informed prior, mixed with the uninformed one); 8 random folds with the DR score is best in all three uninformed cells but still far below the label-matched control (stylised).
Ablating the three changes in ambient-drvalid (score, fold count, fold type): in the uninformed cells random folds help more than the DR score (IPS on 8 random folds is as good as DR on 8), no factor wins everywhere, and every selector stays far below the label-matched control (stylised, negative).
Repeated random fold assignments for cap selection in the ambient-assistant world (follow-up to ambient-drablate): averaging 5 assignments helps the IPS-score selector at ε = 0.02 (3.5 → 5.3 utility/h) and nothing else beyond noise; stylised, simulated only.
Fitting only on the windows an assistant explored at random fixes the uninformed-prior failure of learning from its own feedback (11.99 vs −13.08 utility/h at ε = 0.02), at an exploration cost (stylised)
How many false wakes a day does an always-on trigger get when its frame scores are correlated? Exact grid-chain rates for "m frames in a row" on AR(1) scores, checked by Monte Carlo: a threshold set by the independent-frames rule gives 613 / 4,793 / 20,993 wakes a day (not 1) for m = 2 / 3 / 5 at phi = 0.9, while a single-frame threshold is nearly unaffected. Stylised.
How bursty are an always-on trigger's false-wake counts? On AR(1) frame scores the Fano factor is near 1 (1.05–1.5), but a 5% window-to-window drift in noise scale lifts it to about 9 for m = 3 (38 at 10%); a 10 s lockout cuts it to 2.5 but also cuts the mean by a third. Stylised.
How does the Fano factor of false-wake counts grow with the counting window when the noise level drifts for hours? At 5% persistent drift (about 3 h correlation time) it grows from 1.9 at 100 s to about 150 at 28 h, against a flat 1.9 for independent drift. Stylised; the drift is assumed.
Do a dual-MAC energy loop and a divide-free threshold make the Cortex-M4 voice gate cheaper: 17-37% fewer instructions with the block-minimum floor, slower without it, RAM doubled; decisions unchanged (emulator counts, synthetic audio)
What does the adaptive voice gate cost on a Cortex-M4? ambient-gatefw's C gate built with clang for Thumb-2 and run in an emulator: bit-exact, about 250 bytes of code, 3237 instructions per frame exact and 2096 with the block-10 floor, because the energy sum dominates. Instructions, not cycles; stylised.
Can a noise-adaptive voice gate fit in about 120 bytes of RAM on a pendant microcontroller? C port of ambient-gateroc's adaptive energy gate, bit-exact with the Python reference; a block-minimum noise floor cuts state from 1020 to 120 bytes and comparisons per frame from 249 to 24, moving modelled battery life by at most 0.07 h. Synthetic audio, host build only.
How much pre-roll buffer does an energy-gated audio pendant need to stop clipping the first word? Synthetic audio: no gain in quiet rooms, in the loudest room onset recall 0.866 → 0.980 → 0.999 at 0, 5 and 25 buffered frames (0, 3.1, 15.6 KB) for 90 → 81 → 70 modelled hours; a too-deaf gate is not rescued (stylised)
Does a fixed energy-gate threshold survive different rooms on an always-on audio pendant? Synthetic audio, 20 seeds x 4 background levels: any fixed threshold that keeps speech recall >= 0.9 leaves the gate open all the time in the loudest room (57.6 h, no gating gain), while one adaptive threshold (4x a 5 s running-minimum floor) gives 82-90 h at recall 0.89-1.00 in all four; stylised, nothing measured on hardware
What limits battery life in a pendant-style always-on audio wearable: stylised nRF52840-class power model (mic floor ~170 h; speech-gated ~105 h vs 59 h always streaming) plus a 74-byte VAD gate that compiles for Cortex-M4; no hardware measured
How close can a small shop get to making copies of its own machines? Closure, growth and what to build next, in models that run on a CPU. Topic page →
Part, mass and cost closure of the RepRap Prusa Mendel (iteration 2) for three seed shops: printer alone makes 18 of 51 part lines (35%), plus router and laser 43%, assumed-mass closure 22%; casting helps only with brass bushings. Mass and cost inputs assumed. Stylised.
Which machine a printer-only seed shop should add next under a budget: greedy closure-per-price vs exhaustive search; same choice on the real 3-machine instance, optimal in 72–94% of 500 synthetic instances. Machine prices assumed. Stylised.
Discrete-event and fluid growth of a replicating printer shop with imported vitamins: doubling time falls roughly as 1/budget until machine time binds (about 53 h in the simulation), failed builds cost about 1/(1-f), and closure helps most when imports bind. All inputs assumed; Lackner and Wendt comparison not done. Stylised.
Optimal split of a replicating printer shop's time between copies and goods: copy flat out, then switch one e-folding time (about 50 h) before the horizon; constant splits get 9–27% of that value, smooth ramps no better. Cash-limited cases switch about 50 h from the end. All inputs assumed. Stylised.
Mass and energy balance of plastic and aluminium recycling for one RepRap copy (stylised, assumed process parameters): vitamins stay about 75% of imported mass, recycling the shop's own scrap cuts imports a median 3%, and only retired-machine plastic changes the plastic import much.
Payback of recycling machines with their own assumed part lists (stylised): about 100 printer copies on the shop's own scrap, 12–31 if retired machines' plastic is recycled.
Recycler payback priced instead of weighed (stylised, assumed prices): plastic pair 98–111 printer copies on own scrap, furnace 203, 10–26 with retired plastic.
Closed-form optimal copy share for a replicating printer shop with a saturating goods market (Pontryagin singular arc: goods output grows linearly, last 1/k hours all goods); earns 99.96–100% of the dynamic-programming policy's value. Necessary conditions only; all inputs assumed. Stylised.
Reinvestment of a replicating printer shop when the goods market saturates, checked by dynamic programming: bang-bang is optimal with linear revenue, but with market capacity below about 10^4 machine-hours per hour the optimum ramps the copy share down over 90–300 h and bang-bang loses 4.5–7%. All inputs assumed. Stylised.
Fleet a replicating printer shop sustains when machines wear out (stylised, assumed inputs): short-lived machines die out from one seed; recycling gains need a correction for builds cut short.
Exact mean extinction time of a wearing-out printer fleet as a birth-death chain (stylised, assumed inputs): explains the die-outs in kind, within about 35% only after a post-hoc fix.
Does paying for spares at service start rescue the long repair queue of a printer shop (stylised, assumed inputs): yes, an unbounded queue then beats never repairing (488 against 458 at one bench) and queue caps stop mattering.
Repair labour as a limit on a repairing printer shop (stylised, assumed inputs): with few repair benches an unbounded queue of broken machines is dead stock and does worse than never repairing; capping the queue recovers most of the gain.
Repair versus replacement in a replicating printer shop (stylised, assumed inputs): repair wins iff its cost share is below its success probability, but only if spares are held back from new builds.
How much making its own spare parts cuts a printer shop's repair cost (stylised, assumed inputs): the printer alone makes none of the wear parts, so in-house spares barely move the fleet; the breakdown rate matters more.
Does charging printed spares their print hours erase the printed-bushing gain (stylised, assumed inputs): the fleet ignores waits up to ~500 h per repair because it is import-limited, and the gain was within noise anyway.
Exact Markov-chain test of why a lone replicating printer dies out (stylised, assumed inputs): about a fifth die before a fleet forms at 500 h mean life; wear-out lives remove it.
Quasi-stationary approximation of how long a small replicating-printer fleet lasts (stylised, assumed inputs): within 5% of the exact mean time once a correction for early die-out is applied, poor for the shortest lives.
Reconciles the two exact extinction chains of the lone printer shop (stylised, assumed inputs): the fleet-size chain is 1.5 to 7 times longer; adding the kit wait fixes small fleets but over-corrects large ones.
Which assumed part substitutions (printed bushings and nuts, wooden rods) cut the Prusa Mendel's vitamins most under a penalty budget: all seven take closure from 43/22/16% to 60/36/48% (lines/mass/cost); best set depends on the assumed penalties. Stylised.
Beam model of the Prusa Mendel's smooth rods: a wooden rod sags 20 times a steel one at 8 mm and needs about 17 mm to match it, and selfrep-redesign's assumed dowel mass was twice the geometric one (stylised).
Carriage natural frequency on the Prusa Mendel's smooth rods: a vibration target, not a sag limit, sets the rod diameter; hardwood needs about twice steel's diameter (stylised).
Aluminium rods in the printer redesign: matching a steel rod's sag takes 10.4 mm aluminium (fits the assumed 12 mm holders) against 16.9 mm hardwood (does not), at 39.5% vs 37.8% mass closure (stylised).
Sizing printer rods to a first-mode frequency target instead of a sag spec: at 0.3 kg aluminium reaches 40 Hz with 10.0 mm (fits the assumed 12 mm holders) where hardwood needs 16.0 mm (stylised).
Rod diameter from an acceleration and ringing budget: at 3 m/s² with abrupt steps steel needs 7.3 mm, aluminium 9.6 mm, hardwood 15.5 mm; a 20 ms force ramp cuts aluminium at 5 m/s² from 10.9 to 8.9 mm (stylised).
Which assumed input of the replicating-printer growth model moves its doubling time (Sobol indices, stylised, assumed ranges): budget and vitamin cost together carry ~90% of the variance when imports bind; when machine time binds, failure, print rate, budget and price are comparable.
A resale value s per machine at the horizon shortens the goods phase from one e-folding time 1/k to 1/k − s/a; at s ≥ a/k the shop never switches. Grid optimum matches the closed form. All inputs assumed. Stylised.
A resale value s per machine with a saturating goods market (DP): at capacity c = 1000 machine-hours per hour the copy phase runs to the horizon once s is 12.5 (a quarter of a/k), and the policy that ignores s earns 14% of the optimum; the DP loses to bang-bang by under 1% where the fleet is large, so it is a lower bound there; stylised, preliminary.
Grid-convergence check of the terminal-value DP: the policy's value is stable to about 0.15% from 800 to 1,600 grid points while the table value rises from 8–13% (400 points) to 2–3% (1,600) below it; a stylised fluid model, preliminary.
An interpolation-free DP (the table equals its own policy's value to 1e-14): with no resale value and a saturating market a three-phase policy beats the best single switch by 4.7% (c = 1e4) to 7.1% (c = 1e3), while a resale value of 50 makes one switch optimal; a stylised fluid model, preliminary.
A resale price for the finished fleet that falls with market depth m (stylised): with an unsaturated goods market the switch moves from 574 h (linear) to 549 h (m = 1e3) and a single switch matches the DP; with a saturating goods market the DP beats the best switch by up to 14%.
How much the RepRap closure numbers depend on which parts a shop is judged able to make (stylised, assumed inputs): buying all optimistic lines cuts mass closure from 22% to 17%; making the motors in-house would add 22 points.
Does sharing part jobs across printers beat one copy per printer (stylised, assumed inputs): a pool serving the oldest copy first doubles in 43.2 h against 51.1 h with no import limit, about half the gap to the fluid 34.7 h; with imports binding all policies agree.
How many parts per print plate double a replicating printer shop fastest (stylised, assumed inputs): with no changeover one part per plate wins (43.2 h doubling), with 0.25 h per plate four parts (46.4 h), with 0.5 to 1 h eleven parts; pooled fleets stay 7.6 to 15.5% ahead of one copy per printer.
Designs written as code, simulated, optimised and exported as manufacturing files with an open toolchain, on a CPU. Topic page →
Parametric L-bracket sized by 2D finite elements (scikit-fem) for minimum mass under a stress limit: differential evolution 19.6 g vs random 25.6 g vs grid 31.4 g at equal budget, exported as STL with a printability check. Assumed material inputs. Stylised.
Does greedy substitution search still work past seven items (synthetic instances, assumed generator): 96–100% of the exact optimum on average but optimal in only 33–95 of 100 instances; 64 random evaluations fall to about 89% at 24 items.
With an aluminium rod option priced by sag, the penalty-budget search of the printer redesign picks the 12 mm aluminium rod and reaches 40.0% mass closure at budget 2.0 against 33.1% with the wooden rod (41.4% against 35.8% at full budget); the penalty curve is assumed and the metric favours heavy stock; stylised, preliminary.
Scoring the printer redesign by the mass the shop must still import (vitamins plus raw stock) instead of closure: the best design imports 5.85 kg against 6.72 kg for the baseline, while the closure-maximising 12 mm aluminium pick imports 6.79 kg (stylised; yield and prices assumed).
Which imported printer part to learn to make first (stylised, assumed inputs): by mass or cost the NEMA17 motor (+22 and +26 points of closure, first in 90% and 76% of draws with masses and costs scaled 0.5x to 2x), by unit count the M8 nut; by lines every vitamin ties.
Which process capabilities (lathe, winding, heat treatment, ...) a printer-replicating shop should learn when one capability unlocks several imported parts (stylised, assumed efforts): a lathe is the best first buy by mass (+31 points for effort 4), winding plus stamping by cost (+30 for effort 8), and exact capability sets beat part-by-part picking by up to 10 points, but the choice is fragile to the assumed efforts.
In what order a printer-replicating shop should learn its process capabilities (stylised, assumed efforts): the exact best order over all 362,880 beats walking the budget frontier (54 to 73% of the optimum over 24 weeks); a gain-per-week bundle rule comes within 0 to 6%.
Python reproduction of Sigmund's 99-line SIMP topology optimisation (cantilever, half-MBB; filter removes 11.5% checkerboards) with the density field exported as a mirrored, extruded STL; stylised 2D compliance only.
How much stiffness a topology-optimised cantilever loses when the real load direction differs from the modelled one: 1.57× at 60° and 2.58× at horizontal for the nominal design; a multi-load design at 0, ±60° cuts the worst case to 2.00× for 0.6% nominal cost; stylised 2D, preliminary.
Density filter and Heaviside projection added to the SIMP code: the optimiser's compliance matches the thresholded part's to 0.1% (sensitivity filter: 10% off) but the parts are equally stiff within 0.9%; β continuation needed (β=64 from the start: 344.8 vs 192.1); a minimum-length-scale check found no advantage (negative); stylised 2D.
Does a topology-optimised beam survive a 0.2 threshold error? The plain Heaviside design disconnects when eroded on all three meshes; the robust eroded/blueprint/dilated design stays at 224–226 (14–16% above nominal) for 0.8–3.4% more nominal compliance, but shows no minimum-length-scale gain (negative; stylised).
Does the filter radius or the threshold gap set a robust beam's minimum feature size? A gap of 0.1 already stops the erosion failure (eroded compliance 255–276 against 187–200 nominal; plain design disconnects), but solid feature size is 3 px at both radius 4 and 6 (negative; stylised, one mesh).
Does the minimum feature follow the filter radius once the mesh is refined? No: at 180×60 it is 5 px at radii of 6, 9 and 12 px; across meshes it grows with the grid (1, 3, 5 px), not the radius (negative; two poor 60×20 robust runs reported; stylised).
Does the move limit decide whether a robust topology optimisation survives its β steps? Yes here: at 0.2 five of nine cases failed (blueprint compliance up to 4× the best), at 0.1 and 0.05 none (stylised; mechanism not tested).
Can a move limit that halves after a compliance spike rescue a robust topology optimisation? Partly: fixed 0.2 failed 5 of 9 cases, fixed 0.05 none, the adaptive rule 2 of 9, because it reacts after the damaging step (stylised, one run per cell).
Does rolling back a robust topology-optimisation step that spikes compliance and redoing it at half the move beat shrinking the move afterwards? Mostly: fixed 0.2 failed 5 of 9 cases, adaptive 2, retry 1, fixed 0.1/0.05 none, but retry never beat fixed 0.05 (stylised, one run per cell).
Can penalty continuation free SIMP starts stuck in a different local optimum? No: it sends all 5 stuck starts of 20 to one design (c 204.01) worse than the 202.83 three reach by running longer at p = 3. Stylised.
Is the start-dependence of fixed-penalty SIMP just slow convergence? Over 1200 iterations the median of 20 random starts reaches the uniform-start design (0.0% of elements differ, from 3.9% at 150), but the compliance spread only falls 1.43% → 0.85% (stylised, 2D, one mesh).
How much does a SIMP topology optimisation depend on its starting density field? With a fixed penalty, final compliance spreads 1.4–2.8% over 30 random starts and 2–23% of elements change state; with penalty continuation the spread is 0–0.4% (stylised, 2D, 150 iterations).
How short can SIMP penalty continuation be and still remove the start dependence? A ramp of 25 iterations or fewer leaves much of it (worst start differs in 16–23% of elements, 27–31% for a fixed penalty); 50 iterations cuts compliance spread to 0.01–0.23%, and a 112-iteration ramp is most repeatable but ends at a worse compliance (stylised, 2D, 150 iterations).
Cantilever sizing with Euler–Bernoulli, Timoshenko, 2D and 3D finite elements: stress agrees everywhere, deflection differs; cheap models land within ~5% of the 3D depth, unsafe when narrow and stubby (Euler–Bernoulli) and oversized when wide (plane stress). Stylised, assumed material.
Session-agent design proposals vs CMA-ES, Bayesian optimisation and random search on a bracket sized by finite elements, 40 evaluations each: agent 23.0 g vs 32–39 g baseline medians (best known 22.4 g); the agent had prior knowledge, n = 1, not an LLM benchmark. Stylised.
Manufacturability rules (FDM, CNC routing, laser cutting, sand casting) added to the sized L-bracket: the mass price of each rule set against the same material with no rules (casting +43% from its even-section rule, CNC +24% from plate stock, laser and FDM ~0); designs overshoot the stress limit by 17–26% on a fine mesh (stylised, assumed rule values).
Tension plate with a required bolt hole sized under net-section, Kt = 3 and finite-element stress models and per-process hole rules (stylised).
Does weighting parts by mass change which shop process, and which machine, matters? With a tip load FDM covers 0.30 of parts by count and 0.58 by mass, the laser-versus-CNC order flips, and at budgets 600–800 exhaustive search picks the laser cutter by count but the casting setup by mass (one seed). Stylised, assumed rules and prices, simulated only.
Do the mass-weighting machine-choice flips of simdesign-coverweight survive across seeds? Over 20 seeds, log flips from the laser cutter (count) to the casting setup (mass) in 20/20 at budgets 600–800, large only at 800, small never; the 1100–1400 flips are near-ties (≤0.26 points). Stylised, assumed rules and prices, simulated only.
How wide are the budget bands where mass weighting changes the machine choice when prices are uncertain? With ±20% independent price noise the log flip band widens from budgets 600–800 to 500–1000 but softens at its edges (about one half), and large's single nominal flip at 800 shows up in only 44% of price draws. Stylised, assumed rules and prices, simulated only.
Share of a sampled bracket family each shop process can make under the simdesign-dfm rules: geometry alone adds nothing beyond FDM (negative), with a tip-load requirement the processes separate (FDM alone 30%, +casting +laser 41%) and the best next machine depends on budget and part size, where greedy sometimes loses 1–2 points to exhaustive search (stylised, assumed rules).
Re-runs simdesign-dfm with a stress knock-down and a finer search mesh, checking designs at h = 0.7 mm: the price ordering (casting ~1.4, CNC ~1.23, FDM 1.0) survives the mesh, the laser-cutting price does not (1.01–1.22, noisy), and a 1.3 margin leaves designs at 0.88–1.02 of the limit (stylised, assumed rule values).
Compares peak and patch-averaged von Mises stress under mesh refinement on the L-bracket: the peak rises 18–41% from h = 2.5 to 0.55 mm while a 3 mm patch average moves 1–6%, but it reads only 0.45–0.69 of the peak so needs its own limit (stylised, assumed values).
Repeats the process-rule bracket search with a 3 mm patch-averaged stress instead of the peak: the ordering of mass prices (casting > CNC > laser ≈ FDM) holds, the laser price spread across seeds shrinks from 0.16 to under 0.005, and designs overshoot their limit by 2–12% on a fine mesh against 19–34% for the peak (stylised, assumed values, uncalibrated limit).
Tests whether a near-sharp fillet floor explains the laser-cutting price scatter seen in simdesign-patchsearch: it does not (peak-stress designs already use 7.6–14.3 mm fillets, so floors of 0.2 and 1 mm give identical designs); the patch-stress price is steady (sd 0.006–0.011) at every floor, and the cause of the peak scatter is not identified (negative, five seeds, stylised).
Follow-up to simdesign-filletfloor: the peak-stress price scatter of laser-cutting rules (sd 0.063) sits in the 2 mm gauge sub-search, not the fillet floor; a four-times search budget cuts it to 0.025 but not monotonically, so several nearby optima are plausible but not shown (five seeds, stylised).
Patch-averaged stress for a bolt hole in a tension strip: nearly settled under mesh refinement already, matches Kirsch's disc averages, needs its own limit (stylised).
Checks the finite-element peak stress at a circular hole against Kirsch's exact 3× concentration: the element-centroid peak sits 27% (coarse) to 1.1% (fine) below it and closes only at first order, while hole-edge vertex values are within 1% (stylised).
The peak-stress price scatter of laser-cutting rules is a missed search at the narrow 2 mm gauge (1 seed in 20), not a cost of the rules; stylised, mesh effects untested.
A second DE restart or a doubled population removes the missed 2 mm sub-search (0 misses in 40 runs against 1 in 20 at baseline) and shifts results to the lighter of two mass groups at about twice the cost; stylised, 2.5 mm search mesh only.
The two gauge-2 mass groups differ in web width w (about 14.3–14.9 against 15.2–15.6 mm), not fillet radius, and the lighter group matches ragged isolated feasible pockets on the 2.5 mm mesh rather than a second broad basin; stylised, preliminary.
The isolated feasible pockets of the gauge-2 bracket scan (web width below 15.4 mm) vanish when the mesh is refined from 2.5 to 1.5 mm and the smallest feasible width rises by about 1 mm; stylised, preliminary.
On meshes of 1.0 and 0.5 mm no width in the usable 15.0–16.0 mm window of the gauge-2 bracket scan is feasible (one point at 0.75 mm), and the lowest peak stress rises 11–14% from 1.5 to 0.5 mm; negative, stylised, preliminary.
The whole 1.5 mm L-bracket as one 3D body clears the buckling floor under the design load (factor 4.01 vs closed-form 3.47) but not with the load reversed (2.25, below 3); sharp corner, ideal sheet, preliminary.
Widening the 1.5 mm L-bracket web from 18.4 to about 22.6 mm lifts the reversed-load buckling factor from 2.27 to the floor of 3, at +5.9 g (+19%) plate mass; buckling only, sharp corner, ideal sheet, preliminary.
More element layers through the thickness (1 to 4) move the L-bracket's reversed-load buckling factor by at most 1.2% and the width needed for the floor of 3 by at most 0.07 mm at 1.5 to 3.0 mm gauges, so the thicker-sheet designs of simdesign-revgauge stand; coarse in-plane mesh, sharp corner, ideal sheet, preliminary.
Under the forward 100 N load the four reversed-load buckling-limited L-brackets all clear buckling (factor 4.7 to 5.6), but only the 1.5 mm design also meets the 100 MPa and 4 mm limits; the 2.5 and 3.0 mm designs fail by 2 to 8 times, and the 2.0 mm design passes only on the coarse mesh (95.7 vs 144.9 MPa finer). Stylised.
At the reversed-load buckling floor of 3, a 2 mm sheet needs a web of about 11.8 mm and weighs 27.5 g against 36.6 g for 1.5 mm at 22.6 mm; 2.5 mm gives 20.5 g; buckling only, one element layer through the thickness, preliminary.
Relaxing the 1.2 mm minimum wall of the laser-cut bracket: it does not open 1.0 mm sheet by itself (the buckling floor binds); with floor 1 and wall ≤ 1.0 mm a 24.8 g design appears (unvalidated closed form).
A through-thickness-converged 3D eigenbuckling model agrees with the closed-form buckling factor of the lightest 1.5 mm bracket design to under 1% (3.49 vs 3.47, so it clears the floor of 3); the horizontal-arm formula is about 18% conservative; one design, ideal bar, preliminary.
Replacing the w/b ≤ 8 ceiling with a closed-form buckling-factor floor makes the 1.5 mm laser-cut gauge feasible (31.0 g, about 13% lighter than the best 2 mm design) and changes nothing at 2 and 3 mm; at 1 mm the minimum-wall rule, not buckling, blocks every design; stylised, unvalidated factor, preliminary.
A closed-form lateral-torsional buckling check of the laser-cut bracket arms (stylised, unvalidated by FE): at 2 mm gauge the governing safety factor is 6.9–9.0 for w = 16–20 mm, so the widths of simdesign-widerweb are not buckling-limited, and the factor rises with w, opposite to the w/b ≤ 8 rule; at 1 mm the old rule admits designs below 1.
A 3D scikit-fem eigenbuckling check of the bracket-arm closed forms (stylised, mesh not converged): within about 1% for the governing vertical arm, conservative by 6–29% for the horizontal arm at the 2 mm gauge.
Mesh refinement of the 3D eigenbuckling check of the bracket arms (stylised): refining length, width and thickness lowers every FE/closed-form ratio by 0.9–1.3 points, so the governing vertical arm agrees with the closed form to within 1% (ratio 0.99–1.00 at the finest mesh).
How the 3D eigenbuckling model compares with the slender-beam closed form as a bar gets longer (stylised): the finite-element load is 14.5%, 7.4%, 3.8% and 2.1% above it at l/w = 3, 6, 12, 24.
How much stiffer a thresholded topology-optimised part is than a uniformly thinned plate across volume fractions (stylised): 26–31% lower compliance at v = 0.3–0.5, shrinking to 14% at 0.8, and disconnected designs below that on coarse grids.
Observed convergence order of the 3D eigenbuckling model on a short bar (stylised): three uniform meshes give order ≈ 2.6 and a Richardson limit FE/closed-form ratio 1.137, so the gap to the closed form is not discretisation error.
Replacing the w/b ≤ 8 slenderness rule of the laser-cut bracket with a lateral-torsional buckling factor ≥ 3 lets the optimiser use the 1.5 mm gauge at w ≈ 18.7 mm, 31.3 g instead of 35.9 g (about 12% lighter), and the guard does not bind at that optimum; the result depends on the assumed factor (no feasible design for factors ≥ 5 at that gauge); stylised, preliminary.
Sweeping tip load (50–400 N) and arm length (60–120 mm) of the laser-cut bracket: the buckling-factor ≥ 3 guard binds only at 120 mm arms (unguarded optimum has factor 1.9; 69 g vs 59 g), while the old w/b ≤ 8 rule costs 14–25% in mass in five of six cases (stylised, two seeds).
A 0.1 mm scan of the feasible edge of the gauge-2 bracket web (nine mesh/radius cases): peak stress is not monotone in w, with residual jitter of 0.9–2.4 MPa about a quadratic trend, the same size as the 0.1–1.7 MPa gap to the 100 MPa limit just below each edge, so the edge is a band of about 0.5 mm and the earlier refinement shift is not separated from mesh noise; stylised, preliminary.
With the assumed slenderness limit raised from 8 to 12.5, gauge-2 bracket webs of 16–17 mm and wider are feasible at h = 1.5, 1.0 and 0.75 mm; refinement from 1.5 to 1.0 mm moves the lightest feasible width up 0.5 mm (about 1 g, 3%); stylised, preliminary.
The isolated feasible pockets below w = 15 mm at the 2 mm laser-cut gauge vanish at 2.0 and 1.5 mm element size, and the smallest feasible w moves up (14.4 to 15.6 mm at r = 14 mm); stylised, preliminary.
The narrow 2 mm laser-cut bracket region is a mesh effect: all 39 designs feasible at h = 2.5 mm fail the stress limit at h ≤ 1.5 mm (peak 1.09–1.27× higher, still rising at 0.75 mm); stylised, negative for the search mesh.
A 3 mm patch-averaged stress converges with the mesh (≤2.2% change from h = 1.0 to 0.75 mm) where the centroid peak does not, and all 39 gauge-2 designs stay feasible; stylised, preliminary.
Does the L-bracket's peak stress at the fillet tangent point converge under graded mesh refinement? Yes for four designs: it flattens at 1.09–1.14× its 1.5 mm value (0.0–1.1% change over the last 4× refinement down to 0.025 mm), so the 2 mm region's mesh dependence is a resolution effect; the 16/15/2 design is marginally over 100 MPa when converged; stylised 2D, no reference solution.
Under a 3 mm patch-averaged stress rule the least-mass laser-cut bracket is the same on a 2.5 mm and a 1.0 mm mesh (gauge 2: 32.31 vs 32.33 g), while the centroid-peak rule leaves no feasible gauge-2 design on the fine mesh; the patch value hardly sees the fillet radius; stylised, preliminary.
Do cheap beam and 2D models rank cantilever designs like 3D finite elements? Yes on 3 seeds of 80 designs: Kendall τ 0.987–0.996 and the 3D-best design always ranked first, even though single-design merit is off by up to 14%; stubby sections agree least; stylised, one load case.
Fashion from an engineering point of view: what garments cost to make, and what materials, mechanics and electronics could do for clothes. Topic page →
Bottom-up cost model for a lined coat applied to two reported designer prices: modelled factory cost is under 15% of price, the assumed markup chain does not close the gap, and a $20–50 replica needs very cheap cloth and labour. All inputs assumed. Stylised.
Position-based cloth drape scores a flat skirt-tube pattern on two synthetic elliptical bodies by strain and waist ease; the best waist is near the body's waist perimeter and a pattern fitted to one body fits the other clearly worse. Stylised; strains depend on mesh and solver.
Marker making as strip packing: on 20 random 8-box markers, shelf heuristics leave 17–20% extra length vs the exact optimum, annealing 0.5%; on two stylised garments, polygon nesting beats box packing at equal budget. Stylised; no seam allowance or multi-ply.
A 1 cm seam allowance cut the stylised shirt's marker efficiency from 0.69 to 0.63 and the skirt's from 0.71 to 0.51; mixing three sizes in one marker shortened it 9%; swapped into the cost model, trench cloth rises from $26 to $33–41 at $7/m². Stylised; sensitivity, not a coat measurement.
Cutting-order planning for a 3-size stylised shirt: laying several garments per marker saves 9–11% of cloth over one per marker; mixing sizes adds 0.4–3.7% in sample, but re-nesting the chosen markers with fresh seeds leaves +0.09%, so it is within nesting noise. Stylised; invented shapes.
Nesting a stylised coat's 10 shell and 5 lining pieces with a 1.5 cm seam allowance gives marker efficiencies of 0.68–0.73 (shell) and 0.59–0.68 (lining) at three cloth widths, below the fixed 0.80 in garment-teardown; its trench FOB moves +9% to +15% at the teardown's own areas. Stylised, preliminary.
How many sizes fit a population? On a stylised synthetic bust/hip population (+-4 cm), an exact size run beats a regular grid by 12 to 25 points at correlation 0.9 but not on fresh people at correlation 0; greedy is within 3.7 points of optimal (stylised, preliminary).
How many sizes does a stretch fabric save? On a stylised synthetic bust/hip population, 10% usable stretch cuts the sizes needed for 80% fit from 6 to more than 8 down to 2 or 3; an idealised upper bound (preliminary).
Fanger/ISO PMV and a two-node model extended with fabric infrared transmittance, emissivity and solar absorptance: indoors, transmittance 0→0.8 is worth ~2.4 °C of comfort at 28 °C; in sun, absorptance dominates. Stylised; assumed fabric properties, no reference for the optical extension.
Cross-checks garment-thermal's two-node model against pythermalcomfort over 108 conditions: core temperature within 0.25 °C, skin temperature mean 0.6 °C (up to 2.1 °C) apart; a comparison of implementations, not of people.
Switches nine design choices one at a time between garment-thermal's two-node model and pythermalcomfort's: variable skin mass fraction, convection coefficient and vasodilation gain explain most of the 0.58 °C skin-temperature gap; a comparison of implementations, not of people.
Adds garment-thermal's fabric optics (infrared transmittance, emissivity, solar absorptance) to the switchable two-node model and re-runs the comparisons under pythermalcomfort's choices: property rankings agree in all four scenarios, sizes within 3% at 28 °C but up to ~2× apart in cool air and in sun; a comparison of implementations, not of people.
The fabric-optics comparison of garment-twonodeoptics run to steady state instead of one hour: the cool-room disagreement between design choices mostly vanishes (stylised).
The closed-to-open bounds of an infrared-gating textile from garment-thermal hold under both two-node choice sets and at steady state: opening the gate cools skin by 0.20–0.25 C at 31 C and keeps it 1.4–1.5 C cooler at 16 C; stylised, preliminary.
A skin-temperature-triggered infrared-gating textile with hysteresis and actuation lag settles to a fixed closed or open state under constant rooms (no chatter, lag only delays the start); gains need changing conditions; stylised, preliminary, mostly null.
Under a single step in room temperature, a thermostat-driven infrared-gating textile beats both fixed states after a step up and tracks an oracle schedule closely (stylised).
A step in metabolic rate (rest to walking) instead of room temperature for the thermostat infrared-gating textile: at 24 C the gate beats both fixed states under one choice set and ties fixed closed under the other, at 28 C staying open is as good as any policy, and a 10 min lag erases the gain after walking stops; stylised, preliminary.
Tuning the thermostat infrared-gating band on training rooms and testing on held-out rooms: a narrow band just below 33.7 C carries over (about 0.01 to 0.06 C better than the untuned band) but chatters, up to 24 switches in 180 min (stylised).
Retuning the thermostat infrared-gating band with an actuation lag (0 to 10 min) and a cost per switch: lag cuts the gain over never switching from 0.23 to 0.15 C (stylised), a switch penalty widens the band and stops the chatter, and under one choice set the tuned band can lose to the untuned one.
A proportional infrared-gating transmittance against the tuned on/off thermostat gate: a negative result, within 0.010 C in every cell because the tuned ramp collapses to nearly on/off, and a softer ramp costs 0.02 to 0.07 C (stylised).
Prices actuation in equal units (one full close-open swing = 1) and asks when a proportional infrared gate beats the on/off gate: it wins in 52 of 80 held-out cells, by tenths of a degree at most, and the gain reverses in the outside rooms at the highest penalty (stylised, preliminary).
Retunes both infrared gates on a wider set of rooms: the proportional gate's outside-room reversal is partly a training-range artefact
Tunes both infrared gates on one person and clothing level and scores them on other clothing and body sizes; clothing matters, body size barely does
A grid search for the best open/closed switching schedule under a room-temperature step shows one toggle suffices and the thermostat gate sits within 0.02 °C of it after a step up, but up to 0.11 °C after a step down (stylised).
Joins garment-thermal comfort shifts to garment-teardown costs: only one fabric treatment helps in each scenario, levers combine sub-additively, and at assumed premiums a degree costs $0.5 to $19 on a replica trench but $3 to $114 on a designer one. Stylised; premiums assumed.
Weights garment-comfortcost's fabric levers by wearing time and adds a gated infrared lever: a fixed infrared-transparent shell pays only with a warm-room majority (above 75.5% of time against the cool room), white never harms, and the gate is chosen only when it costs about the fixed shell's premium or less. Stylised; premiums and wearing shares assumed.
How many home-sewn replica coats until labour cost settles? On a Wright learning curve (assumed first coat 4× an experienced operator, rate 0.85) it takes 20 coats to get within 2× of factory time; the first coat stays under $50 only if your time is valued at ≤$1.45/h. Learning parameters assumed. Stylised.
How much longer must a $2,850 coat last than a $56 replica to win on cost per wear? About 46× with no resale and equal care; needs a median life near 3,100 wears to win half the time. Lifetimes, care and resale assumed. Stylised.
Is a second garment better than a dearer single one? A shell-and-layer pair beats the best single garment at the same budget in 54 of 66 wearing mixes at $50 and $100 (mean +0.49 C and +1.02 C) once thin cloth is removed; the apparent $20 gain is an artefact of thin cloth's negative assumed cost. Stylised; premiums and wearing shares assumed.
How often can a wearer pick the wrong garment before a second garment stops paying? With random wrong picks the pair's edge over one garment holds (+0.57 C at 30% error, $100); if every mistake is the worst option it falls from +0.55 to +0.09 C (stylised).
RF-shielding weave model: 54–87 dB sheet shielding but the aperture bound caps it (36 dB at 2.4 GHz for 1 mm pitch, ~15 dB at 28 GHz); yarn breakage tracks 1/(1−2f) and conduction fails near 50% broken. Stylised; plane wave, ideal crossings, RF part only.
Contact resistance at yarn crossings in the RF-shielding weave: no effect on an intact fabric, but with 20% of yarns broken a contact equal to one segment raises sheet resistance 22% and ten segments 2.3×. Stylised; contact values are a sweep, not measured.
Correlated damage in the RF-shielding weave: worn contacts next to breaks (rc×10) raise the median sheet resistance at 20% broken from 2.05 to 3.03 segments; a fold band across the current direction at the same mean breakage leaves 57 of 60 draws open, while a fold along it helps. Stylised; wear multiplier is a sweep, not measured.
Thin-film transfer-matrix structural colour on a nylon-like substrate: 6-pair stacks reach 99% reflectance with 2–3 g/m² of oxide but blue-shift 48 ΔE by 60° incidence, and 10% layer-thickness error moves hue by ΔE≈10. Stylised; flat substrate, no dispersion.
Optimising 8-layer thin-film stacks for low angle shift at fixed colour: Nelder–Mead restarts cut mean ΔE76 shift from 12.4 to 1.4 (red) and 25.9 to 5.6 (blue) at 3000 evaluations, beating random search and differential evolution, at the cost of chroma and ~1.8–2.5× oxide mass. Stylised; flat substrate, no tolerance.
Thickness-error robustness of the garment-stackopt angle-stable stacks: the nominal optimum (J 1.4) degrades to 24.9 at 3% layer error and loses to the quarter-wave stack; a sampled robust objective at equal cost recovers part of it (red, 3%: 11.7 vs 13.2 quarter-wave) but not colour drift. Stylised; independent Gaussian errors, 10 seeds.
Negative follow-up to garment-stackrobust: a CVaR (worst-quarter) training objective and a correlated rate-drift error model do not rescue the optimised angle-stable stacks; none beats the quarter-wave stack (red, iid error: mean J 14.1 vs best optimised 16.5). CVaR trims Nelder-Mead's 90th-percentile cost (47.1 to 43.1) at the price of the mean. Stylised; no coating measured.
Shift against chroma and oxide mass for the garment-stackopt 8-layer coating: on a grid of chroma floors and mass caps, the best red-target shift is 0.68 at a 4.0 g/m² cap but 2.71 at 3.0 and no feasible run at 2.0 or below (floor C* 40); mass binds before chroma. Stylised; 5 seeds per cell, one optimiser.
Layer-count sweep (2 to 12) of the constrained structural-colour coating: six to ten layers reach best angle shifts under 1 dE at C* 40 and 4 g/m2 where 2 and 4 layers stay near 3.4, but 12 layers did not search well at the same budget (stylised, 8 seeds).
One-joint ankle exosuit model: active assist cuts modelled whole-body cost 3–14% (gain 0.1–0.5) but a few kg of garment mass erases it; break-even mass ∝ 1/(mass sensitivity). Stylised; assumed constants, no OpenSim/MyoSuite.
Adds a motor and battery mass model to the ankle exosuit: at an assumed 8 N m/kg the motor (about 8 kg) makes a gain-0.3 suit raise cost 0.2–1.9%; the sign flips between 8 and 20 N m/kg, battery hours matter little. Stylised; assumed constants.
Moves the exosuit's motor and battery from shank to waist: the waist layout wins once a shank kg costs more than 1.03–1.39× a waist kg (assumed ratio, swept); at ratio 3 and 8 N m/kg shank +20.7% vs waist +3.3%. Stylised.
Replaces the assumed Bowden efficiency with the capstan law exp(-mu*theta): at ratio 3 and mu 0.1 the waist layout beats the shank layout until the cable bends through about 31 rad, so friction loss alone does not decide the layout (hysteresis not modelled). Stylised.
Cunniff-style scaling for nylon, aramid and UHMWPE: at equal weight UHMWPE gives 1.49× aramid's V50 and needs 0.20–0.67× the areal density depending on an unknown exponent; a 3 mm, 1 kg suit-like panel falls short of a 4 kg/m² aramid reference except under optimistic assumptions. Stylised; recalled formula, assumed properties and prices, no protection claim.
Activity recognition from simulated chest/thigh/wrist IMUs and knee/elbow strain: two sensors reach ~99% and all five 99.9% on easy synthetic classes, but a clean-trained model falls to 45% under 1 rad garment slip (94% when trained with slip). Stylised; invented signals, no real dataset.
Small accelerators designed together with the model for one task: accuracy, cycles, area and energy per inference, checked in open RTL flows. Topic page →
Keyword-spotting accelerator: quantised MLP on Speech Commands, serial-MAC RTL bit-exact against an integer reference, accuracy vs cycles, cells and modelled energy over width and weight bits (stylised).
A streaming keyword-spotting engine with no weight memory, exact against an integer reference and synthesised to SKY130 on 32 geometries (6,300 to 24,500 um2); 16 hidden units at 8-bit weights is the most accurate (0.616) that fits one assumed 1x1 Tiny Tapeout tile at 70% utilisation, 64 units at 4 bits (0.738) needs two. Stylised: synthesis only.
Model-first vs joint choice of model and MAC lane count under a latency deadline, on the 40 measured accel-kws models; accepting 2 validation points less cuts engine area 31–42% (stylised, table-based, cycles for more than one lane analytic).
NSGA-II against random search at equal budgets on a 3,840-design keyword-spotting accelerator space with exact ground truth; NSGA-II finds 54 to 89% of the exact front at 20.8% of the space against 19 to 21% for random search, though hypervolume is 0.97 to 1.00 for both. Stylised.
Sweeps NSGA-II's population, mutation rate and crossover on the accel-nsga space; mutation 0.02 to 0.1 finds about 0.38 and 0.71 to 0.77 of the exact front at 400 designs, against 0.28 and 0.59 at accel-nsga's setting and 0.13 and 0.12 for random search (stylised).
Weight-, output-, input-stationary and reduction-tree dataflows of a P-lane MAC array on the 40 accel-kws models, from a cycle-by-cycle schedule simulator that matches closed forms exactly and the P = 1 RTL cycles; output-stationary wins on SRAM energy at batch 4 until an input buffer is allowed, then input-mapped flows win at 32 lanes (stylised, assumed energy constants, no RTL for more than one lane).
How large a bounded LRU activation buffer must be before output-stationary stops being the best dataflow for the 40 accel-kws models at batch 4: 32, 64 and 128 words at 8, 16 and 32 lanes (for 10 to 30 of 40 models, input-stationary wins), and not at all at batch 1; buffer-read energy is assumed and no area is charged (stylised).
P-lane output-stationary and reduction-tree matrix-vector engines in Verilog, bit-exact against NumPy at 1 to 32 lanes, with RTL cycles equal to accel-dataflow's schedule model plus a constant 2 or 3 at every point, tails included (stylised, generic-gate area, batch 1, no memories).
Output- and weight-stationary batched RTL engines at batch 1 to 16: bit-exact, cycles and operand-fetch counts equal accel-dataflow's schedule model, and weight-stationary's saved weight fetches cost up to 4x the generic gates (stylised, P = 8, no memories).
Breakeven price ratios from accel-planebatch's RTL counts: register-file weight-stationary beats output-stationary only if an idle flop costs under ~1% of a weight fetch per cycle at batch 4 (falling ~1/B); no energy constant measured (stylised).
Places accel-fetchprice's breakevens against SKY130 liberty energies (idle flop 46 fJ per cycle; OpenRAM macro 10 to 90 pJ per access): with weights packed into SRAM words register-file weight-stationary loses to output-stationary at nearly every batch; partial sums in SRAM lose everywhere. Library values, not measurements.
Prices clock-gated register-file weight-stationary scheduling from SKY130 and GF180 liberty files: an idle clock gate costs 0.86 of an idle flop (SKY130; 0.99 to 1.02 in GF180), so one gate per 24-bit accumulator cuts the idle cost about 28-fold and flips register-file WS from losing to winning against packed SRAM weight fetches in 35 of 64 cells, in all but one cell at 24 flops per gate. Library values, not measurements.
The clock-gated register-file weight-stationary engine in RTL and SKY130 synthesis: bit-exact, same accumulator writes as output-stationary, clock-pin energy 1.0 to 1.07x OS with a gate per set, but area only 7 to 18 % below ungated WS and 1.2 to 5.3x OS (stylised).
The gated weight-stationary engine's lane count swept from 2 to 16 (32 ran out of synthesis memory): bit-exact, clock-pin energy 1.01 to 1.07x OS with a gate per set at every P, area 1.6 to 1.9x OS at B = 4 and flat from P = 4, so the verdict depends on the batch, not the lanes (stylised).
Why the gated weight-stationary engine needed so much synthesis memory: one variable-index read of the accumulator bus; an AND-OR read mux gives bit-exact, same-cycle engines 17 to 28 % smaller, gated WS 1.5x OS area at B = 4 and 2.2x at B = 8 (was 1.6 to 1.9x and 2.9 to 3.0x), and lets P = 64 synthesise (stylised).
Second-node verdict for clock-gated register-file weight-stationary scheduling from IHP SG13G2 liberty files (idle flop 34 fJ, clock gate 0.75 of a flop, ten SRAM macros with separate read energies): one gate per accumulator makes WS beat OS in all 120 cells, but ungated WS also wins 33 of 60 packed cells because IHP's SRAM costs 72 to 497 flop-cycles per weight against SKY130's 18 to 62. Library values, not measurements.
Does accel-gatedmux's accumulator-read bug also inflate accel-planebatch's WS area? No: the rewritten engine is bit-exact with identical counts and its area is within -3 % to +12 % with no trend (WS/OS 1.62 vs 1.66 at B = 4); the earlier verdict stands.
Accel-plane's output-stationary and reduction-tree engines at 1 to 32 lanes through Yosys and nextpnr-ice40 on an iCE40 UP5K: output-stationary at 16 lanes is fastest that fits (10.2 us per 64x70 product, 2,942 of 5,280 cells); DSP mapping cuts logic 13 to 41% but fails to place beyond 8 lanes. Stylised, synthesis only.
Does a quantised surrogate make a design search cheaper in FE solves than searching with the simulator alone? At 150 FE evaluations a surrogate-assisted loop is 2.3 to 2.8 % from a best-known design against 6 to 8 % for an FE-only evolution strategy and 14 to 20 % for random search (float and 6-bit surrogates indistinguishable; stylised, 8 seeds).
With a locking-free Q6 finite-element simulator, how much surrogate error can a design loop tolerate? At 64x8 the surrogate adds 0.5 to 0.8 points to the FE's 2.3 % error; with no safety margin a min-mass screen breaks the limit in 24 to 33 % of cases, with a 5 to 10 % margin 2 to 9 %. Stylised.
When the beam simulator is a 2D plane-stress FE model, does a quantised MLP surrogate (and an accelerator) pay? The energy break-even is met (34x at 32x4 mesh, 319x at 64x8, assumed constants), and the surrogate's 2 % error against its FE is small beside the FE's own 9 % discretisation error; but the locking Q4 simulator is itself inaccurate. Stylised.
Can a quantised MLP surrogate of an FE cantilever beat the Euler-Bernoulli vs Timoshenko gap (0.09 % median), and would an accelerator pay? No: float error is 1.7 % (18x the gap), 6-bit QAT stays within 0.3 points of float, and the surrogate only beats the solver above ~1,600 simulator flops. Stylised.
Can a small behaviour-cloned control network meet the control-rate deadline on a microcontroller or a P-lane accelerator for a two-link arm? Stylised and preliminary: the int8 policies track 300+ times worse than their teacher, so policy accuracy, not hardware speed, is the limit; the latency model (assumed constants) shows hardware matters only above about 10 kHz.
The accel-kws serial-MAC engine through Yosys and nextpnr-ice40 on UP5K and HX8K for 15 geometries (random weights, synthesis only): all fit in at most 22% of the UP5K's logic, weights land in block RAM, Fmax 15–22 MHz on UP5K. Stylised; no board, no power.
Pruning, int4/int8, ternary and binary MLPs on scikit-learn digits (substitute task) with a modelled-energy engine: when does the accuracy slack let the hardware drop multipliers? Stylised; at 1–2 points tolerance, pruned int8 still beats multiplier-free.
accel-sparse's pruning, int4/int8, ternary and binary sweep re-run on real Speech Commands MFCC features: no multiplier-free design is within 5 points of float32 (ternary 19 down), where digits said 1; int8 pruned 50% is the cheapest within 2 points. Stylised, untuned negative.
Weight-sharing product-table inference against int8 MAC engines on the digits MLP: negative at this size, break-even only for wide layers with cheap table reads. Stylised, modelled energy.
Product-table inference on trained wide digits MLPs (32, 128, 512 hidden): at best 14% under int8 energy, only with an assumed cheap table read. Stylised, modelled energy.
Fine-tuning the shared values of accel-lut's product-table engine: rescues K=2 in the 75%-pruned digits MLP (14% under int8 energy only at an assumed cheap table read), not the dense network. Stylised, modelled energy.
The product-table engine and a serial MAC engine in Verilog, bit-exact against NumPy and synthesised with Yosys: negative, the table needs an accumulator per output (stylised)
Classifier-only energy of two-stage keyword-spotting cascades vs 40 single MLPs retrained on the original Speech Commands v0.02 (5 seeds, 200 models, about 41,000 cascades per seed, thresholds chosen on validation): cascades cut modelled energy by 0 to 28% at the same validation target, losing 0.3 to 1.4 test points, and the saving is under 1% of a system whose MFCC front end costs about 50 times the classifier
An instrumented Q15 MFCC front end (512-point FFT, 40 mel bands, DCT) costs 7,532 multiplies per 20 ms frame against the 5,184-MAC accel-kws classifier per inference; under assumed 45 nm constants the front end is 8 to 150 times the classifier's power, and 16-bit FFT scaling decides its accuracy (synthetic frames, no Speech Commands)
A shared data-chosen exponent for the 16-bit FFT in accel-frontend's MFCC path cuts cepstral error to 0.016 to 0.081 of the spread at -60 to -30 dBFS (one shift per stage: 0.35 to 0.72) for about +0.5% modelled energy, but no better than 18 to 20-bit fixed schedules on loud input (synthetic frames, no Speech Commands)
All 34 energy constants in the accel-* projects that have a counterpart in Horowitz's Fig. 1.1.9 are within 4% of it; re-costing accel-kws with the figure's array-size law (energy about the square root of size) moves energy to 0.23 to 0.81 of as built but keeps 17 of 18 front designs (Spearman 0.991)
Pricing every array by its own size flips accel-lut's negative result once read energy grows faster than size^0.26 (dense) or size^0.28 (pruned); Horowitz's slope is 0.5 above 8 KB but there is no point below it, so the verdict is conditional
OpenRAM's clk0 figure is an average power in mW over one cycle of an unstated period, not pJ: the unpacked verdict (register-file WS wins) holds for any period above 3 ns, while the packed verdict flips between 1 and 31 ns, so accel-pdkprice's packed conclusion is conditional
Joining accel-cascade's committed results with accel-frontend's 46.8 nJ per frame: cascades' classifier-only saving of up to 28% becomes at most 0.42% of whole-system energy, while the most accurate model (about 0.75 test accuracy) costs 23 to 26 times the cheapest classifier but only 5% more system energy (modelled, not measured)
Synthesising the streaming keyword-spotting engine at 96, 128, 192 and 256 hidden units (SKY130 HD, Yosys): area grows about 250 µm² per unit, so H = 128 (0.752 accuracy, 4-bit) needs a 2x2 tile (75,603 µm²) against a 1x2 (36,347 µm²) for H = 64 (0.737): +0.015 accuracy for twice the tile; H = 256 needs 4x2 at 50% utilisation, and its 8-bit layer-2 accumulator overflows 20 bits on a random model.
All 96 retrained keyword-spotting models fit the Tiny Tapeout engine's 16-bit bias and 20-bit accumulator limits (worst use 43% and 30%), accuracy through the tile contract equals the reference, and 32 trained models run bit-exact in RTL.
Tiny Tapeout's real SKY130 tile sizes (1x1 is 161 × 111.52 µm = 17,955 µm², 0.43% below the value assumed earlier) applied to the synthesised keyword-spotting engine and the retrained models: the best 1x1 model is unchanged at 100% and 50% utilisation and flips at 70% (H = 16, 4-bit, 0.596 instead of 8-bit, 0.616, a 29 µm² miss); H = 64 with 8-bit weights (0.737) fits a 1x2 tile.
Chip-design loops that need no LLM: algorithms propose designs and flow settings, open tools score them. Topic page →
Unattended design loop (lint, bit-exact RTL sim, gate-netlist check, Yosys synthesis, hash cache, JSONL log, pluggable proposers) run on chip-accel's 40-design grid: synthesis and the gate check are 99% of wall time (stylised, generic-gate counts, no place and route).
Does a space-filling grid order beat the harness's lexicographic one on other families? Lexicographic is arbitrary (worst on MAC, best on FIR); farthest-point beat random from about 6 evaluations on every table, and eda-harness now offers it as an option (stylised, two 36-design families).
Does the order a grid walks a design space matter? The harness's lexicographic grid trails every random order to 30 evaluations; Halton reaches 90% of the front in 7 evaluations against 17 for random (stylised, one table, deterministic orders are single draws).
Random, grid, annealing, GA, NSGA-II and TPE at equal budgets by Pareto hypervolume on an 80-design logged space: TPE and NSGA-II lead random from about 16 to 30 evaluations, annealing trails it (stylised, tiny space, untuned).
A three-rung fidelity ladder (analytic model, RTL simulation, synthesis) over 40 logged designs: the free rung ranks the objective at Spearman 0.74, and successive halving finds the optimum at 20 s of tool time against 205 s to synthesise everything (stylised, toy design family, no place and route).
A cell-count surrogate from cheap word-level RTL features over 133 designs in four generator families: 3.9% median error on families it saw (non-negative linear model), 11% to 210% on a held-out family with rank agreement staying at Spearman 0.75 to 1.00, and it cuts syntheses to find a near-best design in a 36-design pool from 12.4 to 1-5 (stylised, synthesis-only target, no place and route).
Few-shot adaptation of the eda-surrogate cell-count model to an unseen design family: one synthesised design from the new family cuts the linear model's median error from 49% to 18%, training on the new family alone beats pooling from about three designs, boosted trees need about 12 (stylised, synthesis-only target, no place and route).
Which few designs of a new family to synthesise when adapting a cell-count surrogate: a farthest-point spread in feature space roughly halves the linear model's error against random draws at 5 designs (5.3% against 8.5%), the smallest designs are worst, and upweighting new points helps linear and ridge but not boosted trees (stylised, synthesis-only target).
eda-adaptpick's adaptation-design choosers re-scored on one fixed test set per family (4 families x 5 splits): the farthest-point spread still beats random draws for the linear model at every k (4.8% against 6.0% at 5 designs, w = 5) but wins in only 65% of cells, the smallest-first rule stays worst, and the earlier 'halves the error' margin shrinks to 20-45% at 5 to 8 designs.
A cell-count surrogate used as a screen in the design-search loop: 4 spread syntheses plus a log-linear fit reach 0.990 of the true front's hypervolume at 12 syntheses against 0.860 for random and 0.878 for TPE, of which about +0.05 comes from free cycles/error objectives (stylised, one 80-design space).
With Gaussian error on the objectives a proposer sees, TPE's budget-30 lead over random falls from +0.037 to +0.006 (gone at error 0.8 of the objective range), NSGA-II and the genetic method lose theirs by 0.1, annealing is never better (stylised, synthetic noise, one 80-design space).
TPE stays best under five hypervolume reference points, recall, IGD+ and epsilon, but its lead over random at budget 30 ranges from +0.045 to +0.002 with the reference point (stylised, one 80-design space).
A random search that uses the free cycles/error objectives reaches 0.901 of the true front's hypervolume at 12 syntheses (random 0.860, screen 0.990), so +0.04 of the screen's lead is the free objectives and +0.09 the cell-count surrogate (stylised, one 80-design space).
A Pareto screen whose cell-count model was trained only on other design families reaches 0.94 to 0.98 of the true front's hypervolume with 3 Yosys syntheses (random about 0.65), though the model's absolute error is large; ranking is what matters (stylised, MAC and FIR spaces of 27 designs).
All 400 ABC pass sequences on eight small SKY130-mapped designs: one design's best recipe scores a mean 1.31× the other's optimum, and a transferred warm start helps only one design (stylised, toy designs, no place and route).
Mutation study of random, coverage-directed and bounded-formal RTL checks on the MAC accelerator: 64 random vectors kill 99% of killable mutants, formal 71% (timeouts), at ~50x the CPU cost (stylised).
Replays the eda-verify mutation log to cost check cascades: random simulation before formal cuts CPU by 54% with more kills; the order among cheap stages barely matters (stylised re-analysis).
Replays the eda-verify log with a time cap on formal: a 170 s cap loses no kill and saves 41% of cascade CPU but forfeits every equivalence proof; a 230 s cap keeps 15 of 16 proofs and saves 23% (stylised re-analysis).
Predicts from the mutated source line which simulation survivors formal can prove equivalent: nearest-line prediction cuts formal CPU 55% and finds 14 of 16 proofs on one design (stylised, 27 mutants).
Puts a line-clustered interval on eda-equivpredict's 93%: 25 of 27 survivors right, 95% CI 76.5–100% over 11 distinct lines, permutation p = 0.012 (stylised, one design).
Tests whether an identical post-synthesis netlist predicts formal equivalence on a second design (systolic array) as well as the MAC engine: right 3 of 3 times but finds only 3 of 28 proved equivalents (stylised, two designs).
Tests whether Yosys netlist features (cell-count change, miter size) predict which eda-verify survivors are provably equivalent: none beats the 59.3% majority class under leave-one-line-out, against 92.6% for source line (negative, stylised, one design).
Fan-in cone features (changed sinks, cone gates and depth, registers reached) from hashed gate-level netlists vs which eda-verify survivors are provably equivalent: none beats the 59.3% majority class under leave-one-line-out (best 13 of 27; negative, stylised, one design).
eda-adaptfixed re-run with 40 splits per family and bootstrap intervals: for the linear model the spread beats random draws at every k (about 1 point of error at 3 to 8 designs, 2.5 at 2), but for ridge it loses at 3 designs and one family (sorter) reverses the sign, so the pooled interval is narrower than the real uncertainty.
eda-adaptci re-run with a design-level bootstrap: the intervals widen by up to 2.5x, the spread's lead holds at 5 and 8 designs for both models (about 0.5 to 1.1 points) and at 2 for the linear model, but the linear k = 3 lead and the ridge k = 2 lead include zero, and the ridge k = 3 loss reported earlier is not established.
The eda-adapt few-shot curves refitted to OpenROAD-placed area on 133 SKY130 designs: an unseen family's placed area is off by 39% (ridge), one placed design cuts it to 23%, about three reach 20%, as for cell counts.
Four biased generators (20,000 vectors per target) catch none of the 26 eda-deepdraw survivors, so none contradicts a formal equivalence proof, and the del@122 mutant is confirmed as truncated output (90 rows for 100 vectors).
The 40 MAC-engine designs mapped to SKY130 at six shared clock targets: cell count still ranks area (Spearman 0.995+), logic depth ranks delay at only 0.34 to 0.82, and with one shared clock the Pareto front equals the generic one, so the earlier front change came from per-design clocks.
20,000 further random vectors catch none of the 25 eda-verify survivors, so none contradicts a formal equivalence proof; a random-visible bug among the 9 formal timeouts has per-vector detection probability below 1.4e-4.
Library-free delay proxies on the generic gate netlist of the 40 MAC engines: gate-type weights leave depth's Spearman 0.611 against SKY130-mapped delay unchanged (0.609), adding fan-out lifts it to 0.83 to 0.90, but gate count alone reaches 0.911, and no proxy recovers the true (area, latency) front.
Per-vector detection probabilities of the eda-verify mutants: a geometric model fits the random-vector miss rate within 0.005, predicts 45 vectors for a 1% miss, and 1,280 clean vectors cannot rule out a bug rarer than 0.0023 per vector (stylised re-analysis).
Five golden-free properties (latency, done pulse, output hold, start-glitch and reset-abort invariance) kill 22 of the 66 killable eda-verify mutants, all control-flow bugs, and none of the 15 ROM or other datapath bugs; the 16 directed vectors catch all 22 too.
A generic-gate cells × cycles screen puts the best SKY130 area × latency design first among 40 MAC engines; over random pools of 20, mapping 3 designs finds the pool's best 97% of the time, against 15% for random choice.
The 40 MAC engines placed with the pip OpenROAD wheel: ABC area still ranks placed area (Spearman 0.997+), ABC delay only 0.61 to 0.80, wires add a median 36% to the period, and no design ABC calls feasible at 5 ns meets it after placement.
Across 207 cheap screens of 40 MAC engines, Spearman agreement with SKY130-mapped latency does not predict top-k screening payoff (−0.13 at k = 1): the highest-Spearman screen (0.958) maps the best design first 32% of the time, gate count (0.551) 69%; for area × latency it does (0.60).
Searching generic-gate objectives instead of SKY130-mapped ones (RMS error 0.036 on area, 0.123 on latency) costs within 0.01 of hypervolume on the 40 MAC-engine designs, and TPE's +0.037 lead over random at budget 20 is unchanged.
A screen with cost models trained on other families finds the placed (OpenROAD, SKY130) area-period front in 3 to 6 placements where random reaches 0.92 only at 16, but the true fronts hold only 1 to 2 designs, so the test is easy.
The 40 MAC-engine designs mapped to the SKY130 HD cell library: generic cell count ranks mapped area at Spearman 0.995 but logic depth ranks mapped delay at only 0.611, so the (area, cycles) Pareto front is unchanged while the (area, latency) front loses one design and gains another.
Z3 bounded model checking via yosys-smtbmc decides none of the 10 undecided eda-deepdraw survivors at the 24-cycle depth a full inference needs; its cost passes from about 3 s at depth 10 to over 240 s at depth 12.
The 24 systolic-array and MAC-lane designs of chip-systolic mapped to SKY130 at six shared clocks: the MAC-lane engine keeps the best area x latency at every feasible target (arrays 1.61 to 1.66x worse), though the clock removes many arrays and changes the Pareto front.
Cost per good die from five yield models, a dies-per-wafer count and sourced wafer prices and defect densities: a 600 mm² die costs about $179 on a 7nm-class and $359 on a 5nm-class wafer, the yield model moves the 5nm figure by 16%, and two chiplets beat one die from about 300 mm² of logic (range 126-728 mm² over packaging cost and defect density).
Milestones 1 to 3 done: on 10 designs x 60 ABC pass sequences, the generic-gate score does not rank like routed SKY130 area x delay (tau-b median -0.04), and liberty mapping mis-ranks too when the clock is tight (tau 0.59); at equal wall-clock a one-shot cheap-rung screen does not beat random or hill-climbing search on the cached table; successive halving across rungs does not beat random routed search on mean regret either (plain halving from the generic-gate rung is worst; a 6-point routed pilot to pick the start rung fixes most of that, H3), a 10-point routed pilot plus a conformal bound on the mapped rung keeps the routed optimum 0.99 of the time (nominal 0.90) at 42 to 57% of the routed runs, but on the generic-gate rung coverage fails (0.65 against 0.80, H4 refuted there); proof-success prediction (H5): pooled AUC 0.96 to 0.998 across 15 designs is just design size (an oracle knowing only each design's success rate scores the same), and inside the one design with variation it is 0.65 to 0.78, so H5 is not supported; milestone 6 proves that halving's routed regret is at most the sum of the cut rungs' largest ranking inversions (vacuous for the generic-gate rung, loose for the mapped ones); milestone 7a adds a distribution-free pilot quantile of pair inversions (16-point pilots hold the nominal 0.8 coverage in all 60 group-rung cells, median 0.32 of the maximum), whose summed bound is under 0.1 on 9 of 10 groups for the mapped rungs at a relaxed clock but is violated by realised halving regret in 1 of 40 cells, so it is a heuristic, not a guarantee
Robots built for one job and designed from the task outward: when a specialised body beats a general-purpose arm, on cost, speed and reliability. Topic page →
When does a purpose-built gantry beat a general two-link arm at tray pick-and-place? At 2 mm tolerance the arm wins only between 0.36 and 0.99 m of work area, and the band depends on assumed costs (stylised).
Does co-designing an arm's link split and controller beat tuning the controller on a fixed body? Co-design gained 1.9% in held-out move time (0.283 against 0.289 s), within three-seed noise; tuning the controller mattered about 37%. Stylised, preliminary, mostly negative.
Can a small twin of a liquid-handling bench catch protocol errors before they run, and how much pipetting error does a serial dilution tolerate? It flags 366 of 522 injected faults against 100 for a syntax-only baseline, and an assumed error curve gives a final-well CV of 0.187 at 10 µL and 0.035 at 100 µL transfers (stylised, circular fault set).
Does the real Opentrons simulator catch the faults the stdlib liquid-handling twin catches? On the same 522 seeded faults it raises on 270 and the twin flags 366; everything the simulator catches the twin catches too, while tip reuse, a 5 µL dispense and a half-empty source pass the simulator. Mostly policy differences; the fault set was written for the twin (stylised).
Does searching a planar arm's joint count, links and mount, with its controller tuned, beat a fixed three-link body at equal cost? On a shelf task with a tool-down constraint, 0.95 held-out success against 0.26; on a long position-only reach, no gain (stylised, kinematic).
How heavy must a purpose-built UAV for targeted observation be, and when is a hover-capable airframe worth its weight? At 3 km out and 20 min on station a fixed wing closes at 1.27 kg against 2.14 kg for a quadrotor and 2.08 kg for a VTOL wing, and the quadrotor stops closing at 45 min (stylised, assumed constants, no flight stack run).
Does a steady wind change which purpose-built observation UAV is lightest? At 3 km and 20 min on station the fixed wing stays lightest from 0 to 18 m/s (1.27 to 1.50 kg) while the quadrotor goes 2.14 to 7.0 kg; the multirotor's still-air win at 1 min on station ends near 10 m/s. Stylised, steady known wind only.
How much heavier must an observation UAV be if the wind is uncertain? Designing to the 95th-percentile of wind ~ N(8, 3) m/s costs the fixed wing +3.7% and the multirotor +11.7% mass, and a bigger battery reserve buys about the same reliability for about the same mass; stylised, one steady wind per mission.
If an observation UAV launches only when the forecast wind is under a limit, how much does forecast error bring failures back? A perfect forecast turns every failure into a scrub (fixed wing, wind ~ N(5, 4) m/s: 4.6% scrubbed at the 95th-percentile limit); a 2 m/s error gives 6.8% failures at the median limit but 1.1% at the 95th. Stylised, one steady wind per mission.
If a scrubbed observation-UAV launch can be retried later the same day, how much does persistent wind limit the gain, and do retries bring failures back? Fixed wing, median-wind limit, perfect forecast: eight slots complete 99.7% of days with independent wind but 71.5% with persistence 0.95; with a 2 m/s forecast error eight slots raise failures from 6.8% to 13.6% of days (23.7% at persistence 0.95). Stylised.
What is a UAV launch wind limit worth in money, and should the launch threshold sit below the design limit when the forecast is wrong? With an assumed expensive airframe and a 2 m/s forecast error the best threshold sits 1 to 6 m/s below the design limit, worth up to $284 per attempt, with failures at or below 0.1%; with a cheap airframe the best design covers nearly every wind. Stylised, assumed prices.
When does one shared robot beat a dedicated robot per job in a pick-and-place shop? Sharing wins while the total load fits one machine and changeover is short (4 jobs, trays within 0.4 m: shared cheapest at demand 0.2 per job, dedicated from 0.3); the shared arm often cannot hold tight tolerances. Stylised, assumed costs.
What does a shared pick-and-place robot cost once it must stay up? Spares priced per job or for every job at once: the shared fleet costs the same fraction of a robot per job when its load fits one machine (0.68 at 4 jobs), and falls to 0.34 to 0.51 when all jobs must run at once. Stylised, assumed availabilities.
What sets the force on the lips when a spoon-feeding arm meets a swaying mouth: the sensor, the approach speed or a force cap? Peak force tracks approach speed (1.0 N at 0.05 m/s, 4.0 N at 0.20), a camera cuts how often the lips are touched (0.40 against 0.72 of trials) but not how hard, and latency erodes that gain. Stylised point-mass model, assumed constants.
Does a spoon-feeding arm need more than two joints? From 2 to 6 joints the tip mass moves only 0.63 to 0.50 kg and lip force not clearly at all, while servo cost triples (stylised; extends osrobot-assist).
Does the stylised feeding-arm lip-force result survive MuJoCo contact physics? The steady push matches KP × LEAD × speed, but the impact peak is 1.84 × higher and the share fed at most 2 N falls from 1.00 to 0.45 at 0.10 m/s (stylised; extends osrobot-assist).
Is the peak force of a feeding arm on the lips set by lip stiffness, the force loop or the approach lead? Lip stiffness moves the mean peak from 0.32 to 2.02 N at 0.20 m/s (stylised; extends osrobot-assist).
If the person being fed judges the spoon better as it nears the mouth, how much of a camera's value does a blind arm get back? A misjudgement shrinking to zero at the lips lifts the blind arm's safe share at 40 mm from 0.47 to 0.84 and restores every feed; stylised, extends osrobot-leannoise.
If the person being fed misjudges the spoon or sees it late, can a blind feeding arm still do without a camera? A 20 mm misjudgement drops the blind arm's safe share from 1.00 to 0.60 (camera arm 0.78); stylised, extends osrobot-lean.
If the person being fed leans toward the spoon, can a blind feeding arm do without a camera? At 30 mm sway and 0.20 m/s the blind arm's safe share rises from 0.21 to 1.00 as the lean reaches 100 mm/s (stylised; extends osrobot-assist).
When a pest window sets a deadline, is a scout-and-treater fleet or inline weeding robots cheaper? One scout cannot finish 16 fields faster than 5.3 to 32.5 h; pipeline/inline cost is 1.06 to 1.12 at 0.72 ha, 1.49 at 0.18 ha, and 0.87 to 0.93 at 1.62 ha where it can meet the deadline.
If one scout drone feeds ground treaters in a pipeline, can a held fleet beat inline weeding robots? One scout keeps only 1.0 to 1.3 treaters busy; overlapping the stages cuts the held-pair penalty to 1.04 at 0.72 ha fields and 0.86 at 1.62 ha, still losing on small fields. Assumed prices; scheduling over osrobot-pairprice's fits.
Is a scout drone plus a camera-less ground treater cheaper per hectare than one weeding robot? With assumed prices and each machine charged for its own minutes, break-even is near 0.5 ha and the pair is about 0.7 times the cost per hectare at 5 ha; held for the whole job it never wins; flips with utilisation, labour and battery life. Stylised, nothing built.
Does a fast scout platform plus a ground treater beat one weeding robot? At matched kill (0.343) a 3 m scout swath finishes in 26.6 min against about 42 min for one inline robot, but a 1 m swath takes 47.3 min; a mud-aware tour changes nothing (stylised, simulation only).
Does a better tour rescue scout-then-treat weeding? 2-opt cuts the tour from 539 m to 468 m but a field still takes 56.1 min against 51.7 min treating inline; scouting loses at every weed density tried (stylised, simulation only).
For a weeding robot with a cheap camera, is it better to treat weeds as it drives or to scout first? Scouting then touring killed the same share (0.399 against 0.401 at 1 m/s) and was slower in all 23 paired rows; lane overlap repays a weak sensor (0.40 to 0.86 killed) at 3.5 times the time. Stylised, constants assumed.
Research programme (proposal stage): pump-shaft energy of fixed open-centre, load-sensing and ideal independent-metering circuits on an illustrative excavator cycle; over 2,916 swept cases load-sensing uses a median 47% of open-centre energy and metering 80% of load-sensing, an ordering that holds by construction; on 20,000 random cycles in a machine envelope load-sensing is a median 44% of open-centre; no measured cycle, margin or price is sourced yet
On 115 scripted COLREGs encounters a rule-aware velocity-obstacle planner passes at least 100 m in 95.7% (rule-based 77.4%, sampling MPC 84.3%), but its safe share falls to 82-85% when the target's velocity estimate is off by 0.3 to 0.6 m/s, and the stand-on vessel's action range matters most: 91% at 200 m, 99% at 600 m
Research programme (proposal stage): energy per survey kilometre of hull types for 100 to 500 kg autonomous boats; with a Michell wave term a catamaran out-ranges a monohull in 3.3% of 6,561 cases, none at equal length; with Slocum coefficients from the gliderflight package a glider never out-ranges a same-mass propeller AUV at equal hotel load (0 of 2,430 cases); it breaks even when the AUV's hotel load is about 5 times its own; a REMUS-100-class AUV's non-propulsion load implied by vendor endurance is 104 to 175 W, far above that, so the glider out-ranges it in every case on energy per metre (at a tenth of the speed); a Savitsky planing hull reaches at most 0.14 of the monohull range (0 of 48 cases); a SWATH (two submerged torpedoes on struts) out-ranges the monohull in none of 4,374 swept pairs; charging panel mass to the battery (2 to 10 kg/m2, swept) cuts the median solar range multiplier from 2.01 to 1.64 at worst, and the full deck stays the best array wherever range is finite; against ten years of daily NASA POWER insolation a threshold speed policy (slow or hold when the pack is under 30%) never raises km/day over a fixed 1 m/s but cuts pack-empty days, e.g. 25.4% to 1.5% for a 4 m boat at 25 N
Plain line-of-sight guidance leaves a steady cross-track offset of delta*tan(asin(c/U)) in a cross current c (simulation matches it to 1%: 3.77 m at 0.3 m/s, 12 m look-ahead); integral LOS removes it, with lower rms cross-track error in 136 of 144 cross-current cases and the 8 exceptions all at a 6 m look-ahead with integral gain 2, where it oscillates (rms about 2.3 m even in still water)
Replaces the hard deadline of osrobot-deadline with a 2% yield loss per leaf stage of delay (Knezevic et al. 2003): the best pipeline costs 1.06 to 1.20 times the best inline fleet at 0.72 ha and 1.49 to 1.51 at 0.18 ha, and at 1.62 ha inline is cheaper when the window closes by 8 h and the pipeline from 12 h
What does a 2-joint feeding arm cost against a 6-joint one once the whole bill of materials is priced? About 1.8 times, not 3: $66 against $122 at the SO-ARM101 table's $13.89 servo, rising to 2.4 times at a $49 retail servo.
Re-running the osrobot-field weeding model with sourced laser-weeder constants (2 m swath, 0.73 s per weed, 99.2% kill) halves the time but keeps the ranking: inline treatment takes 71.7 min against 79.3 for scout-then-treat at 0.3 weeds/m² and 1 km/h, and scout never wins across densities, speeds and detector hit rates
Can a stdlib static linter catch the lab-protocol faults the Opentrons simulator accepts? It flags 362 of the 522 seeded faults to the simulator's 270, adding reused tips, tips left on, sub-minimum volumes and carry-over; stylised, partly circular.
At the ISO/TS 15066 face stiffness (75 N/mm) the blocked-arm impact peak only doubles (7.56 N against 3.68 N at 0.10 m/s), and every camera-arm trial stays under the 65 N and 130 N face limits (worst peak 53 N), where the assumed 2 N limit had flagged most; contact damping is unsourced and swept (MuJoCo, simulation only)
With tissue as a 5 to 20 mm layer bonded to bone at 4 to 45 kPa, the force that indents it 30 % is 0.05 to 9 N, 1.3 to 1000 times below the simulated 12.6 to 53 N trial forces, so the arm needs a newton-scale force cap, not 65 N (published bottom-effect corrections, no FE run)
Published in-vivo face and lip moduli are 4 to 45 kPa, below the 0.05 to 5 MPa that osrobot-mjpress swept; at them a 4 mm tip at 53 N would sink 48 to 241 mm in a Hertz model, so the model is out of range and tip radius or depth, not 65 N, is the design question (closed-form, simulation forces)
A 4 mm feeding-arm tip that meets the 65 N face force limit still needs 0.5 to 2.7 cm² of contact to meet a 110 to 20 N/cm² pressure limit at its worst trial (53 N); the answer flips on an unsourced face modulus (MuJoCo, simulation only)
Replacing the 75,000 N/m spring with a bonded tissue layer (4 to 45 kPa, 5 or 15 mm) cuts simulated peaks to 1 to 3 N in most cells but still breaks the 30 % depth limit in about half the trials; a 0.2 to 0.5 N cap fixes steady pushes, slowing to 0.02 m/s fixes a 10 kPa, 15 mm lip, and nothing fixes a thin 4 kPa one by speed alone (MuJoCo dynamics, closed-form tissue force)
How fast can a purpose-built robot fill a 96-well plate, and does the robot or the number of channels matter more? Eight channels cut the time by 86 to 88 % (9.5 s against 69.7 s for a gantry at 10 µL) while gantry against arm moves it 4 to 14 %, since about 76 % is fixed pipetting actions (stylised; every speed, price and accuracy figure assumed).
Re-runs osrobot-deadlineloss with a Holybro X500 V2 drone (609 USD) and an AgileX Scout Mini (4,500 USD) at list price: pipeline over inline cost moves from 1.49 to 1.54 at 0.18 ha and 1.07 to 1.15 at 1.62 ha, ties at a 4,500 USD ground platform, and flips with an unsourced loaded flight time
Does the osrobot-uav multirotor energy model match real aircraft? With the Mavic 3's published 9.4 in propellers (0.239 m) it predicts 1.3 to 1.6 times the published 45 min endurance, so it is optimistic; the Anafi UKR rotor size was not found, so that row remains a sweep.
A laser-weeding robot that drives three fast passes (4 km/h) kills 0.780 of the weeds in 75 min, against 0.607 in 83 min for one slow pass (1 km/h), and treating on the move instead of stopping cuts time by 6% at 0.3 weeds/m² and 39% at 3 weeds/m²; the ranking survives 30% of weeds being invisible to the detector
With a detector fitted to two published field detection rates (88.9% at 0.2 m/s, 86.2% at 0.425 m/s), two laser-weeding passes at 4 km/h kill 0.952 in 40 min against 0.875 in 68 min for one pass at 1 km/h; the ranking holds, and the share of weeds the detector never sees (3 passes cap at 0.897 with 10% hidden) now sets the ceiling
Measuring and optimising the agent loop that builds this portfolio: what the run log records, what a run costs, and which work is worth the budget. Topic page →
Where do agent runs say the documentation hurts? 714 doc_friction entries from 1,015 runs: two files hold 39%, and most classifiable complaints name a (file, theme) already reported on an earlier day. Preliminary.
Do documentation complaints repeat more than chance? A permutation null for the swe-friction repeat rate: 171 of 418 classified entries repeat an earlier-day pair vs a null median of 238, so complaints repeat less than chance. Preliminary.
Which test input should you use to calibrate a mass-spring-damper twin? A resonant sine gives the lowest held-out prediction error (3.1e-4 vs 1.1e-3 for a step) yet the worst Fisher condition number (527 vs 56 to 114); fitted spreads sit within 0.83 to 1.09 of the Cramér-Rao bounds. Stylised, preliminary.
What can the run log measure about the agent loop today? Cost fields are present in at most 1% of 189 runs, a third of listed projects are follow-up families, and every recorded CI-failure count is zero. Preliminary first step of track 10.
What does an agent run cost, and which cost the most? 355 priced runs (14 to 18 October): median $0.68, total $337; the top 10% hold 36% of spend; cost grows with tool calls to the power 1.18 (preliminary; API-equivalent estimates).
What do agent runs record going wrong? 17% of 1,027 runs record an error (24.5% of research runs); environment 28%, own mistakes 21%, collisions 17%; runs with an error end partial twice as often (12.6% vs 6.0%) and cost about twice as much. Preliminary: keyword classifier, self-reported.
Do the swe-errors keyword rules sort run-record errors correctly? On a 60-entry blind hand-labelled sample they agree on 40 (66.7%, Wilson 54.1% to 77.3%; kappa 0.59); the ci-or-tooling rule never wins and own-mistake recall is 55%, so the earlier shares are a lower bound for those two. Preliminary: one labeller.
Can the swe-errors keyword rules be improved on 30 hand labels and still help on the other 30? A two-fold held-out refit (rule order plus greedy keywords) averages 68.5% agreement with the hand labels against 66.7% for the shipped rules (+1.1 entries over 200 splits, range -4 to +7), while the same procedure scores 85% on its own 60 training entries: mostly memorisation. Preliminary.
Did research brief v1 change how runs go? Same-days comparison of v0 (342 runs) and v1 (67) on 15 to 18 October: no detectable difference in cost, time or success; the lower v1 error rate (7.5% vs 17.0%) vanishes within unlabelled-task runs (8.3% vs 9.6%); v1 records more doc-friction entries (1.24 vs 0.72 per run, p = 0.0001). Observational.
Does Opus pay for itself on this portfolio's runs? An Opus run costs about 8 to 9 times a Sonnet run in the same track; with 12 priced Opus runs the ledger cannot compare value per dollar, and a 50% difference in projects per run needs about 129 runs per arm (preliminary; cost only).
Do agent runs that record a deviation from the brief cost more or end worse? Of 1,564 run records 203 list one; within track they take ~1.6x as long and cost ~1.2x as much, but the cost gap rests mainly on the process track, and they end partial 5 points more often. Observational, preliminary.
How well does a run's tool-call count predict its cost? On 882 priced run records cost is about $0.03 per call, a log-log fit has R² 0.91 and a held-out median error of 9%; the pooled slope 1.22 is partly group mixing (1.10 within Sonnet). Preliminary.
Where does a run's cost go? On 893 run records with per-token-kind usage, cache reads are a median 45% of the API-equivalent cost and 1-hour cache writes 41%, output only 13%; the starting context (about 60,000 tokens) is re-read on every request, which makes cost grow faster than linearly in tool calls (preliminary).
Do agent runs that add no tests end worse? 84 of 621 counted run records add none; within track they end partial 4/84 against 16/537 (+2.6 points, p = 0.23, no detectable effect) and cost less, probably because they do less. Preliminary.
Which kind of recorded deviation predicts a partial outcome? Of 213 run records with a deviation, tooling failures end partial 22.6 points more often than runs with none (track-stratified p=0.001); skipped steps (+1.3) and switched tasks (+1.3) do not. Keyword classes, observational, preliminary.
How complete are the agent run records, field by field? Of 1,362 records, cost, tokens and wall time are present on 47% (0-7% on 13 to 15 October, 61-82% since), merged on 4.6%, and 18.5% of success runs name no pull request (preliminary; presence, not correctness).
Does a bigger run buy more output? Across 157 priced run records that report adding tests, cost and tests added rank together pooled (Spearman 0.57) but weakly within research runs (0.19), and the dearest third yields the fewest tests per dollar; preliminary, tests added is a crude self-reported proxy.
What does a run cost per merged pull request? 366 priced runs joined to main's merge history: 75% name a merged PR, $1.26 per merged run against $0.94 per run, process runs about 2.4 times research's; red team never links its PR (preliminary; API-equivalent estimates).
What does git history say about the agent loop that the run log cannot? All 157 projects created since 2026-10-13 are in the log, the 217 it lacks are pre-log bulk output, and at most 3% of fully observed projects have a correction-worded follow-up commit. Preliminary second step of track 10.
Can two passes agree on what a project is worth? A three-level value rubric scored two automated ways over 408 projects agrees at chance (kappa 0.07, 95% 0.01 to 0.13), partly from a name-family flaw fixed after the fact (0.25); a blind 30-project hand sample agrees better (0.45 to 0.57, wide intervals). Preliminary, track 10 milestone 3; no correctness term.
When can a prompt experiment stop? Fixed-n, peek-every-pair and a mixture SPRT simulated on ledger-shaped outcomes: peeking declares an identical brief different in 21% (success rate) to 40% (value) of experiments, the mixture test stays under 5% but needs far more runs than a 97% success rate allows. Stylised, no candidate brief run; track 10 milestone 6, partial.
Which track should the next run work on? Four allocation policies (uniform, greedy, bootstrap Thompson, knapsack-UCB) replayed offline on 7 tracks' scored projects: greedy and Thompson reach about 80% of the best-arm oracle against 60% for the current uniform pick, but value per line falls with order in 4 of 7 tracks, so the stationary replay overstates the gain. Stylised, offline only, no live trial; track 10 milestone 4, partial.
How much of the track-allocation gain is luck of the history? Block bootstrap of the sequential replay: at 20,000 lines greedy and Thompson beat uniform in 98–100% of 200 histories (intervals exclude zero), knapsack-UCB's does not; the small-budget loss does not reproduce. Stylised, offline only; follow-up to swe-decay.
Do track-allocation gains survive when tracks run out of projects? Sequential, no-replacement replay: at 20,000 lines greedy and Thompson keep most of their lead over uniform (pass A 134 and 130 against 114), but at 5,000 lines they lose to it (24 against 30). Stylised, offline only; track 10 follow-up to swe-allocate.
Do committed results reproduce? A seeded sample of 40 projects with a runnable experiment was re-run: 36 (90%, 95% Wilson 77% to 96%) matched their committed results.txt, 3 timed out under load and 1 needed a missing voice model. Preliminary first pass of track 10, milestone 2; it checks reproduction only, not citations. Second sample of 60 (92 distinct projects pooled): 81 reproduced (88%), no finished run differed; re-running the 5 timeouts serially reproduced all, giving 86 of 92 (93%).
When research merges collide cleanly, is the result still right? None of 92 clean replays was broken (28.7% of pairs within 60 min conflict); found and removed two duplicate README bullets the build missed.
How long do research pull requests stay open, and how often do they really collide? Median 0.9 min open (95% merged within 30 min); replayed from real creation times, 2 of 58 shared-file PRs (3.4%) conflict.
Does a research branch live longer than its pull request, and which shared file collides most? Median 1.1 min from first commit to merge (vs 0.9 for the PR); research/PROJECTS.md conflicts in 5 of 44 PRs that edit it, more than the index files (3 of 58).
Do sibling research projects ask different questions? Same-family projects overlap in Question wording about ten times more than cross-family ones (Jaccard 0.078 vs 0.008); preliminary, a crude proxy.
How often do research merges collide on the shared index files? 64% of merges edit both; a later merge within 30 min of an earlier one conflicts textually in 18.6% of 59 replayed pairs (assumed branch times, preliminary).
How many parallel agent runs duplicate each other when they start together? 12.8% of runs at four blind starts; a start gap past the claim latency or scheduler slots remove it (stylised, assumed timings).
Do concurrent runs pick the same track more than chance, and is the pick uniform? Measured from git: the whole-period skew is track availability, uniform is not rejected once all eleven tracks existed (36 PRs, low power), and the same-track excess among overlapping PRs vanishes after controlling for drift (preliminary).
What do 526 closed pull requests say about how the agent loop lands work? 87.5% merged, falling to 81% in the tracked era; PRs opened within 10 seconds of another merged 60% vs 92% (association only). Preliminary third step of track 10.
Which practices of engineering organisations that ship could help an agent loop? A cited catalogue of 61 practices from 60 sources (batch 22 adds Microsoft's Nudge reminders for overdue pull requests; batch 21 adds Uber's merge queue that keeps main green; batch 19 adds Sentry's LOGAF-marked code review; batch 18 adds Mercari's tiered production-readiness checklist and Apollo's priority-ordered load shedding; batch 17 adds Kohavi, Tang and Xu on controlled experiments and Strathern on measures that become targets; batch 14 adds Reason and Vaughan on organisational accidents; batch 13 adds Rigby and Bird on lightweight review, Humble and Farley's deployment pipeline and Beck's Extreme Programming), scored against the 1,261-run ledger: no new proposal clears a 5% ceiling (negative, preliminary). Ongoing, with a research log; track 10, milestone 7.
Do agent runs that start alongside other runs, or at certain hours, go worse? Raw, crowded starts look better (error recorded 9.8% vs 21.0%) but that is a day effect; shuffled within days there is no detectable difference over 660 timed records, and hour of day shows nothing (negative, preliminary, low power).
Do parallel review sessions duplicate each other? 6 of 35 review-track PRs (17.1%, Wilson 8.1–32.7%) are the second of a pair merged 0.4 to 2.5 minutes apart, and 5 of 6 pairs edited the same generated files; cost unmeasured (3 of 35 priced). Preliminary.
Do the agent run records match git? All 522 records naming a pull request in this repository name one that landed, but only 79.8% of sessions landing commits from 13 October have a record (ventures 79.2%, research 92.2%; preliminary, seven days).
Why do landed ventures sessions leave fewer run records? 79.6% against research 92.2%; scope, size and kind explain nothing, the ventures sub-prompts alone omit the record step, and coverage rose from 53% to 84–89% in a week (preliminary).
How often does this portfolio report a negative or mixed result? In an 80-summary hand-labelled sample, 59% of the summaries that test a claim against an alternative (43–73%) report a negative or mixed result (preliminary, one labeller).
Do later projects build on earlier ones? A reference graph of 723 READMEs: 61.7% of projects are named by at least one later project (Wilson 58% to 65%), inbound counts are very uneven (Gini 0.69) and 71% of references stay within a track; naming is an upper bound on reuse.
Does an Opus agent run cost more than a Sonnet run on the same kind of work? Matched on date and track, 6.3× the cost (CI 4.7–8.0), 3.2× the tool calls and 2.0× per call; 1.4× per self-estimated human hour. 46 Opus vs 958 Sonnet runs, preliminary.
On 1,053 priced run records (16 to 21 October 2026) the median research run grew about 4.9% a day in API-equivalent cost (95% interval +2.8 to +7.0) and 5.7% a day in tool calls, while cost per call stayed flat; ventures runs show no drift (preliminary, observational, six days)
Does a cheaper start fix the small-budget loss of smart track allocation? One forced pull per track removes it on the observed history (33 against uniform's 30 value points at 5,000 lines) but not provably on resampled histories; a shrinkage rule is no better than uniform on the observed order and matches the others on resampled histories.
Can a frozen language model be prompted to write like people, against a detector that is also only prompted? The context suite, the reference detectors and the game loop. Topic page →
How well do prompt-free detectors tell people from a plainly prompted LLM, and do they carry over to unseen kinds of text? Eight RAID families split by family: n-gram detector AUROC 0.93 and Binoculars-style 0.80 on held-out families, length at chance. Preliminary first step of track 11.
Do this repository's file sizes follow Benford's law? Not as a whole (byte MAD 0.018, nonconforming) because templated files repeat the same size thousands of times; counting each distinct size once gives acceptable conformity (MAD 0.0068).
Can prompt search alone move a frozen 0.5B imitator past a prompted 0.5B detector? A stylised first run of the imitation game, four proposers at equal budget on two families: the starting detector is below chance, proposers cannot be ranked at this size, and length is a major confound.
Does the prompt-only imitation game settle or cycle? Every imitator prompt from mimic-loop against every detector prompt (0.5B on both sides): pure equilibria below chance (reddit 0.396, reviews 0.292), no cycles at a noise margin, and text length tracks detector accuracy. Stylised, one loop seed; model-size question open.
Does a prompt-free n-gram human-vs-machine detector hold up on context families it never saw? Detector side of mimic-anycontext with no LLM (model download was blocked): AUROC 0.934 on unseen families against 0.985 in-family, and 40 target items close most of the gap on recipes. Stylised: plain-prompt RAID text only.
Which features let a human-vs-machine detector carry over to a context family it never saw? Leave-one-family-out AUROC with train-only vectorisers: words 0.931, characters 0.916, both 0.938, function words alone 0.797, surface formatting 0.687 (below chance on abstracts and recipes), length alone 0.155 to 0.885 depending on family. Stylised: one classifier, plain-prompt RAID text, no LLM.
Can a prompt make a 0.5B model detect machine text, and does it carry to unseen families? Negative: the prompted Qwen2.5-0.5B detector is inverted (mean AUROC 0.278 plain, 0.293 universal on held-out families, none above 0.5 on any family) while the n-gram detector gets 0.93. Stylised: one small model, 16 prompts, plain-prompt RAID text.
Does MAUVE rank human-vs-machine gaps the way a text detector does? Across 20 RAID family × model cells MAUVE (lexical embedding) and a cross-fit n-gram detector agree loosely (Spearman −0.60) and disagree on recipes and news; every cell is far below the human-vs-human null (0.92 to 0.99). Preliminary, no GPT-2 features.
Can cheap surface edits (typos, contractions, no chat preamble) fool the n-gram human-vs-machine detector? Most move held-out AUROC under 0.005; 2% typos cost 0.012 and keeping half the text 0.051 (from 0.927), and a refit detector wins it back.
How many words must an imitator change to evade a word n-gram human-vs-machine detector it can read? Deleting the 20 most machine-ward word types per text takes held-out AUROC from 0.948 to chance (0.487); a refit detector recovers to 0.94-1.00.
How many detector queries does an imitator need to evade a word n-gram human-vs-machine detector it cannot read? About 100 score queries per text, deleting the 20 best word types, take held-out AUROC from 0.948 to 0.520 (white-box 0.487); blind deletion does nothing. Stylised, no fluency check.
Does refitting a text detector on attacked text stop a black-box evader? It settles after one refit: fresh-attack AUROC stays near 0.81 (from 0.719) while clean AUROC falls from 0.948 to about 0.90. Stylised, no fluency check.
Does a prompt-free detector carry over to a generator or decoding it never saw? The mimic-contexts n-gram detector loses 0.01 to 0.02 AUROC on a chat model left out of the fit (0.96 to 0.98 left out) and 0.025 to 0.05 on a left-out decoding (sampling 0.936); averaging over four same-source texts lifts AUROC to 0.999. Preliminary, plain-prompt RAID text only.
Does adding a zero-shot perplexity score to the n-gram detector help on unseen families? The two scores are uncorrelated within class, but averaging them lifts held-out AUROC only from 0.926 to 0.935 (paired gain +0.009, interval −0.010 to +0.026); fitted stacks do no better. Preliminary, 720 held-out texts, small scorer, no LLM run.
How much text does a prompt-free detector need, and what does it key on? The mimic-contexts n-gram detector on held-out families: AUROC 0.65 at 50 characters, 0.84 at 400, 0.93 at 1500; stripping punctuation or shuffling words costs at most 0.014. Preliminary, plain-prompt RAID text only.
If a detector's threshold is set for a 5% false-positive rate, does it hold on an unseen text type? Leave-one-family-out with the mimic-contexts n-gram detector: realised rate 0.00 to 0.54 (abstracts 0.54, books 0.18), and recipes catch 1.7% of machine text. Preliminary, plain-prompt RAID text only.
How many human texts does it take to re-set a detector's threshold for a 5% false-positive rate on a new kind of text? About 80: with the plain 95th percentile k = 20 gives a mean false-positive rate of 9% (36% chance above 10%), k = 80 gives 6.1%; a conformal rule holds 4.9% but costs recall and needs 19+ texts. Stylised, RAID text, one n-gram detector.
How many texts from one source does a weak human-vs-machine detector need before a batch verdict is reliable? Four all-machine texts give AUROC 0.997 (one text: 0.935); a quarter-machine source needs about 32; but a threshold set on 150 human texts drifts from 7% to 15% false flags at k = 32. Preliminary, RAID text, one n-gram detector.
Does a classifier two-sample test catch digital-twin errors that a paired trajectory error misses? Stylised pendulum: boosted-tree AUROC 0.72 for a friction error whose RMSE is a quarter of the sensor noise, 0.92 for Gaussian-vs-Student-t noise at zero paired error. Preliminary, simulated only.
Does a kernel MMD test catch the same wrong digital twins as a classifier two-sample test? Stylised pendulum: raw-trajectory MMD is blind to a Coulomb-friction error (power 0.05 to 0.06) that boosted trees catch from n = 200, but MMD on second differences detects a +25% noise-level error at 0.97 from n = 100.
Does a classifier two-sample test see the integrator, timestep and friction gaps of a MuJoCo digital twin? Stylised pendulum: AUROC 0.98 for Euler at 0.02 s, 0.53 (null) for a paired error of 0.003 rad, 0.92 for Gaussian-vs-Student-t noise at zero paired error. Preliminary, simulated only.
Does a kernel MMD test catch the same wrong MuJoCo digital twins as a classifier two-sample test? Stylised MuJoCo pendulum: boosted-tree C2ST power 1.00 at n = 200 for Euler at 0.02 s and a noise-shape error where MMD stays near 0.05; MMD on second differences catches a +25% noise-level error; friction errors undetected by all at n <= 200.
Does a digital twin that a classifier can tell apart from the real system also make a worse controller? Stylised pendulum: 6 of 15 wrong twins have zero controller regret at C2ST AUROC 0.58 to 0.999; the worst regret (3.8%) comes from a twin with no sensor noise and zero paired error. Preliminary, simulated only.
On a swing-up task where friction matters, does a twin's detectability predict what tuning on it costs? Stylised pendulum: only the two gravity-error twins cost much (3.7% and 8.3% extra real cost); 13 others cost under 0.3% at C2ST AUROC 0.51 to 1.0. Preliminary, simulated only.
Does a finer controller grid change which wrong pendulum twins cost something on the swing-up task? No: the same two gravity-error twins cost 3.8% and 6.1%, the rest under 0.3%; detectability vs regret ρ = 0.38 (p = 0.16). Preliminary, simulated only.
Does a wider gain grid, or a controller that uses the twin's gravity, change which wrong pendulum twins are costly? Gravity errors stay the costly ones; giving the controller the twin's g/L made g/L −20% regret 13 times larger (0.013 to 0.177). Preliminary, simulated only.
Does tuning a controller on a spread of randomized twins cut the regret of tuning on one wrong twin? Stylised pendulum: it brings the no-noise twin's regret from 0.0098 to 0.00006, but a very wide range raises a doubled-noise twin's worst-seed regret 7.5-fold. Preliminary, no LLM.
Does randomizing only the noise level of a wrong twin keep domain randomization's rescue without its blow-up? Stylised pendulum: the no-noise twin's regret goes 0.0098 to 0 and stays small at a wide range (worst seed 0.0015 vs 0.042 for all-four), but friction and gravity errors are not helped. Preliminary, no LLM.
How many real trajectories does a classifier test need to flag a wrong digital twin, and are the twins it flags the ones that cost a controller? Stylised pendulum: all six twins with controller regret of at least 0.001 are flagged by 80 real trajectories, and so are three that cost nothing. Preliminary, simulated only.
Does a second turn make a plainly prompted LLM easier to spot in dialogue? A prompt-free n-gram detector gets AUROC 0.93 on one imitated user turn and 0.98 on two, on 400 OpenAssistant threads with a 0.5B imitator. Stylised baseline, no prompt optimised.
Can an imitator that changes its own code fool a human-vs-bot cursor detector, and does shared feedback help? On DUX cursor strokes of 46 people, a held-out reference detector catches every final imitator at AUROC 0.99 to 1.00 in all four feedback conditions; two-way sharing gave the strongest detectors in cross-play (0.81 vs 0.70 blind, interval includes 0), and an 8x larger search stops at 0.88, the level of replaying real strokes. Preliminary.
Can a generator imitate a person's webcam emotion signals well enough to fool a detector? On DUX Affectiva scores of 46 people, every fixed generator and every loop-tuned imitator is caught at AUROC 0.997 or higher by a detector the loop never saw; only replaying real windows gets close to chance (0.61). Preliminary.
Does giving a webcam-signal generator real heavy tails and bursts fool a detector? No: copula and quiet/burst generators still separate from held-out people at AUROC 1.000 (8 seeds); restoring per-window level and spread brings level and spread to near chance, but extremes (0.995) still give it away; copying a real window's value set (G6) puts those at chance too, yet all-groups AUROC stays 0.998 on temporal structure.
Does a bigger Qwen make a better human-vs-machine detector? Partly: plain-prompt AUROC rises from 0.278 (0.5B) to 0.329 (1.5B), but 1.5B is still below chance in 84% of family-by-prompt cells.
A 1.5B code model rewrites the cursor generator against the mimic-cursor detector: only 25 to 29% of its candidates run, and the reference detector stays at AUROC 1.000, tied with the component search at the same 24-candidate budget (one seed, preliminary negative).
Does a prompt-free detector transfer to unseen generators? Mostly: char+word n-grams keep AUROC 0.97 to 0.98 on a held-out chat model and 0.94 across a greedy-to-sampling shift; function-word cues alone drop to 0.69 to 0.85.
Do the mimic-loop imitator prompts fool detectors they never saw? No: matched on length, all 26 testable prompts are still caught (n-gram AUROC 0.83 to 0.96, Binoculars-style 0.84 to 1.00); low raw scores come from text length.
Can a Markov chain over a person's frames fool a detector? No: chains with 8, 32 or 128 states, fitted on one person or on everyone, emitting state centres or real frames, are caught at AUROC 1.000 (one cell 0.999), where stitching the same real frames in 50-frame blocks scored 0.57 to 0.65.
Does fitting to one person help? Copying a person's own earlier windows is caught at AUROC 0.59 to 0.65 on their later windows; copying other people is 0.58 to 0.91, and 0.93 to 0.97 once the detector knows the person; a fitted parametric generator is caught at 1.000 either way.
Does giving a chain over a person's frames dwell times or second-order memory help? No: semi-Markov and second-order chains (8 or 32 states, own or pooled fit, centre or real-frame emission) are all caught at AUROC 0.999 to 1.000.
Why is block-stitched real webcam signal still caught? With 50-frame blocks random stitching gives AUROC 0.887, one person's windows only 0.687, join-matched 0.796, both 0.588 (= whole-window replay 0.597); at 5 frames all are caught (8 seeds).
Cutting what it costs to design and build a home, with the engineering done as open, testable code and the designs published. Topic page →
How much does advanced (OVE) framing save in a house's exterior walls? Stylised 28 × 40 ft house: 42% less wall lumber and 27% fewer pieces than conventional 2x6, whole-wall R 16.2 to 18.6, studs at 39% of capacity under 30 psf snow; the lumber is worth only $450–900 a house, so labour carries the case. Not a code check. First project of track 12.
How far can a 2x joist, rafter, header or beam span? Open NDS sizing tool, no table copied: 2x10 SPF floor joists at 16 in span 15 ft 3 in, bending governs most floors and snow rafters, deflection most ceilings; deepest joist at 24 in uses 20–50% less lumber (vibration unchecked). Not validated against published tables. Milestone 2 of track 12.
Does a floor-vibration frequency limit erase the lumber saved by deep, widely spaced joists? Beam-theory first-mode frequency on the house-spans checks: limits up to 10 Hz change nothing, 12 Hz shortens a 2x10 at 16 in from 15 ft 3 in to 13 ft 11 in, 15 Hz moves the least-lumber 12 ft joist from 2x10 to 2x12. Joist alone, limit is a policy knob. Stylised. Track 12.
How much of a floor-vibration penalty does the subfloor's T-beam action recover? Gamma-method partial-composite stiffness on house-vibration: at a 15 Hz limit a 2x10 at 16 in grows from 12 ft 6 in to 13 ft 2 in–14 ft 6 in, depending on two assumed inputs (connection efficiency and panel modulus). Stylised.
Does a joist lapped over a middle support span farther than a simple span? FE beam with pattern loading and NDS checks: two-span peak moment equals a simple span's, so bending-governed floors and snow rafters gain nothing; deflection-governed ceiling joists gain up to 18.5%; 1.5 in bearing on the middle support cuts a 2x10 floor joist to 11 ft 4 in. Not validated against published tables. Follow-up to house-spans.
How far can the beam under a two-span joist sit from the middle of the house? Bending-governed floor joists lose 0.4% of total width at a short/long span ratio of 0.9 and 13% at 0.5 (the short span relieves the long one); deflection-governed ceiling joists lose about 5% per 0.1 of ratio. A 2x10 floor can have its beam 3.5 ft off the middle of a 28 ft house. Stylised; not a design.
Can a house plan be data, and which plan needs the least lumber per sq ft? Parametric one-storey plan to framing takeoff, bill of materials, room-rule checks and IFC4; best plans use 4.8 to 5.2 bf/sq ft at 640 to 1,024 sq ft with none feasible by stick framing at 1,400; local search hits the exhaustive optimum in 36 of 40 runs where random search hits none. Stylised, not a design.
Where does a new home's price go, and which levers move it most? Share-anchored model (NAHB 2024): size moves the price most (87.8 to 112.0 for 1,600 to 2,400 sq ft), then storeys, finish level and lot; a 14% framing-lumber cut is worth 0.85% of price (2.4% with labour). Index not dollars, assumed driver splits. Milestone 4 of track 12.
Does the house-cost lever ranking survive its assumed driver splits? Monte Carlo over the splits: floor area stays the largest lever in 96–100% of draws; storeys is the soft claim (swing 9.0–19.9 vs 14.0 baseline); the lumber result does not move. Index not dollars.
Which uncertain input of the house-cost model drives a house's price uncertainty? Sobol indices over every lever range, the framing share and the driver splits at once: floor area 53% of variance, storeys 19%, all framing inputs together under 1%. Index not dollars.
Which envelope upgrades pay back over 30 years, by climate? A degree-day net-present-cost search of 640 packages in eight climates: advanced 2x6 framing is in every optimum (13–15% lower cost than a 2x4 baseline); better windows and R-49 attics do not pay at assumed prices. Stylised, assumed prices, not EnergyPlus.
Does any alternative to a wood-framed wall beat it on cost, carbon or heat loss for a small house? In a stylised model wood 2x6 is cheapest in 97% of random draws and lowest-carbon in 100%; SIP, CLT and printed walls win only on labour. Inputs are ranges from memory.
Does a small wood-frame house have enough shear wall for wind and earthquakes once the openings are cut out? At 115 mph and SDS 0.50 the 28 x 40 ft house uses 19% of a gable-wall line's capacity at 6 in nailing; the openings, not the load, are what shrink it. Stylised, capacities from memory.
How much does accidental torsion add to the garage-front wall's demand in a rigid-diaphragm wind split? Offsetting the load up to 15% of the length in house-nailedwall's split raises a 22 ft-door wall from 0.36–0.59 to 0.44–0.71 demand over capacity, still under the flexible 1.05. Stylised.
Does the rigid-diaphragm relief for a garage-front wall survive a nailed-wall stiffness model? Four-term pier deflection (bending, shear, nail slip, hold-down) in house-diaphragm's rigid split: yes; a centred 22 ft door falls from 1.05 (flexible) to 0.36–0.59 demand over capacity. Stylised.
Does the half-and-half load split understate the demand on a garage-front wall? In a toy stiffness model a rigid roof diaphragm gives the garage line less than half, so the flexible split governs; stylised, torsion not modelled.
What does an open plan set for a 480 sq ft backyard cottage look like when generated from code? A 24 x 20 ft ADU composed from the track's models: drawings, bill of materials, IFC, lateral check, envelope energy (a tight envelope cuts modelled heating and cooling cost 36-37%) and a cost index. A worked example, not a buildable design; every input assumed.
At what climate does each envelope upgrade start to pay? Climate as a continuous axis over house-energy's model: slab-edge R-10 from 3,271 heating degree-days with gas (2,386 with a heat pump), 3 ACH50 from 5,769, and cooling alone switches on only the attic and air sealing above ~3,000 cooling degree-days. Stylised: unsourced prices, no solar gain.
How much extra can a tight envelope cost before it stops paying back on a 480 sq ft backyard cottage? The ADU's whole upgrade package can carry $1,409 to $3,104 of extra first cost (3% real rate, heat pump); at assumed prices only the wall switch clearly pays. Stylised.
Does a tighter envelope let a 480 sq ft backyard cottage use a smaller heat pump? The tight package cuts the design heating load about 36.5%, worth a $450 to $1,800 equipment step credit (assumed catalogue and prices) that nearly closes the payback gap of the costed upgrades in three colder climates. Stylised.
When does cooling, not heating, set the heat pump size for a 480 sq ft backyard cottage? Adding a summer load (conduction, window solar gain, internal gains) shows cooling governs only in Houston (12 kBtu/h baseline, 9 tight); sizes and credits elsewhere are unchanged, and Houston's credit swings between $0 and $900 with SHGC and latent allowance (stylised, assumed inputs).
How much lumber does a prefabricated roof truss save over rafters and ceiling joists? A pin-jointed W truss with NDS checks uses 40-55% less nominal lumber per sq ft of plan than 16 in rafters plus ceiling joists over 12-30 ft spans at 30 psf snow (stylised: no plates, bracing or heel details).
When does building a house's wall shell in a factory beat building it on site? Panel layout, sheathing nesting (1 sheet in 33 saved) and a Monte Carlo of the shell: panelised takes 2.17 d against 1.96 d on site and costs 38% more at assumed rates; it is faster only from about 58 ft long. Closed panels (insulation, wiring, windows built in) cut the gap: cost parity at a factory labour ratio of about 0.45 and a day saved. Stylised, every rate assumed.
Which foundation is cheapest for a small house as the frost line deepens? At 48 in frost a frost-protected shallow foundation is $13.2k against $20.6k slab, $24.1k crawlspace and $54.9k basement in a stylised model.
Does a factory-built shell pay once the interest on the days it saves is counted? Alone it saves 15.5 working days (0.22% of price) and breaks even near a $629,000 house at an assumed $1,500 crane day.
How much do fewer handoffs, parallel trades, early ordering and a factory shell cut a house's build time? Discrete-event Monte Carlo: critical path 100 working days, baseline 214; early ordering -63 d, fewer handoffs -21, a factory shell only -6 unless ordered at day 0 (-78). Stylised, uncalibrated.
Does an independent second schedule model agree with house-schedule? Same ranking (early ordering of long-lead items first, prefab only with it, handoff gap matters), different magnitudes (-11% against -29%): sizes are set by assumptions. Crew-merging does nothing. Every input assumed.
Does the month a house build starts change how long it takes? Same Monte Carlo as house-schedule with a monthly weather calendar: in an assumed cold climate a December start takes 231 working days against 211 for July (~20 d); in a mild one, 4 d. Early ordering saves ~63 d in every month. Weather numbers assumed.
Does solar gain through windows change the cheapest envelope, and is window orientation worth money? Adds first-principles solar geometry to house-energy: U 0.50 stays optimal in 15 of 16 cases, and orientation is worth $420–$1,740 of 30-year cost. Stylised: degree-day model, assumed prices and clearness, not EnergyPlus.
When should a builder order long-lead materials once holding them costs money? Extends house-schedule: ordering ~2 lead times ahead of plan cuts the build from 214 to 182 working days and total cost from 3.34% to 2.91% of price; ordering everything on day 0 saves more days but costs more (4.00%).
Does a roof overhang over south windows pay for itself, and where does it cost energy instead? Adds profile-angle shading of south beam radiation to house-solar; at an assumed $12 per ft of width per ft of projection no overhang is optimal in 8 climates (gross value at most $280 of 30-year NPC, negative past 1 ft in cold climates). Stylised degree-day model.
Where in a wall does vapor condense, and does a vapor retarder or exterior foam fix it? Steady-state Glaser check of a 2x6 wall in four assumed climates; winter condensation appears in Chicago and Duluth only, and only polyethylene clears Duluth. Stylised.
What does a new home cost to build in the US and Colorado in 2026, and where does the money go? Sourced market report: median new US home $393,700 (Aug 2026, −5.8% y/y) while input costs rose 10.3%; NAHB's breakdown puts construction at 64.4% of price and foundations, framing and exterior at 26%, so a 20% cheaper structure moves the price 5.2%; manufactured homes cost ~52% of site-built per sq ft; Denver fees and plan-review delay are ~12% of a modelled $462k (lot excluded) home against 3.5% nationally.
Does the cost-optimal home envelope change when invented fuel prices are replaced by EIA state prices? Optimum unchanged in 10 of 12 cases; 30-year saving moves by −$496 to +$549; advanced 2x6 walls still win and R-49 attics and U 0.27 windows still do not pay. Only fuel prices are sourced.
How much dearer can a heat pump be than a gas furnace plus AC before gas wins on 30-year cost? Break-even premium $84 to $735 in the South; in Chicago to Duluth it would have to cost $5,399 to $6,698 less. No equipment prices used; stylised.
Does a temperature-dependent heat-pump COP change how much more a heat pump can cost than gas before gas wins? Seasonal COP 4.01 (Miami) to 2.30 (Duluth) under an assumed curve, so the constant 2.5 understated the South: break-even premium $156, $952, $1,979 in Miami, Houston, Atlanta and −$8,050 in Duluth; signs unchanged, size curve-dependent. Stylised.
How fast must gas prices rise against electricity before a heat pump ties a gas furnace on 30-year cost? At equal installed cost the heat pump already wins in Miami, Houston and Atlanta unless gas gets cheaper; in Chicago, Minneapolis and Duluth gas must rise 4.6%, 3.7% and 3.7% a year in real terms for 30 years. Stylised.
What does Denver Water's 2026 tap fee cost a 480 sq ft ADU against a house? A flat $2,170 for the ADU against $5,400 for a house charged on 2,000 sq ft, from the utility's own schedule; Denver's own sewer schedule adds $575 (shared water tap) or up to $7,055 (own tap), so about $2,745 to $9,225 in all.
Do the nails carry a hung wall panel? Sheathing-to-top-plate nails take 17–31 lb each (0.20–0.36 of capacity) if they share the load; the closed panel fails when under about 40% of the row acts, and a bare frame's stud end nails get no credit.
Can a crane or telehandler lift the house's wall panels? Weights of the eight house-offsite panels (343–559 lb open, 376–877 lb closed), best pick points and top-plate bending (4–12% of allowable with two picks): bending never limits the layout, weight and wind do. Hand-lifting needs 7–18 people; a 20 ft open panel swings 10° at about 12 mph. Stylised, every density and coefficient assumed.
Mass, energy and CO2 balance of a tonne of cement: OPC 830 kg CO2, LC3-50 491 (41% lower, 39-43% over every swept input), 50% slag 441; the clinker can fall to 50% and keep class 42.5 only if the OPC reference has 55 MPa of strength, to 54% at 50 MPa.
Filming a travel creator from every angle with open, packable hardware and an automated edit: the pixel, perspective, battery and weight limits first, in simulation. Topic page →
How long a lens can a 360 camera fake by cropping into a reel? An 8K equirect is native only to ~24 mm-equivalent at 1080x1920 (85 mm is a 3.5x upscale), and perspective is set by distance: a stick at 0.8 m enlarges a 10 cm-nearer feature 14% vs 7.6% at an 85 mm framing distance, so portrait looks need a camera standing back. Pixel-count upper bound. First project of track 13.
What should a travel creator pack to film from many angles within a weight budget and the 100 Wh battery limit? Exact search over 17,280 kits reaches all 18 band x viewpoint shots at 5 kg; a greedy packer stalls at 12 because lenses need their body (assumed device figures).
How many cameras, and where, to film a person from every angle? A 30° gap between neighbours needs 13 cameras on a ring (15° needs 25), but depth error is set by convergence angle, not count: a pair's error falls 11× from 5° to 90° (7.3 to 0.64 mm) while 3 vs 16 ring cameras only halves it. Idealised 2-D lower bounds.
How far apart can cameras be before a reel editor can no longer synthesise the angle between them? With exact depth a two-view warp beats cutting to the nearest camera only up to about 30° (24.8 vs 23.6 dB); beyond that holes dominate, and a bystander pulls the limit in to about 15° (ray-traced toy scene; ordering, not decibels).
Is the depth a camera rig can actually measure good enough for the in-between angle? Block-matching stereo on rendered pairs feeds the two-view warp: mean depth error 14.9% at 3 cm baseline to 2.7% at 50 cm, coverage peaks at 91%, and the result never beats cutting to the nearest camera (22.3 vs 24.8 dB at a 15° gap; exact depth 27.3 dB).
Can the holes and correlated errors of measured stereo depth be repaired so in-between synthesis beats cutting to the nearest camera? A hole filler and a no-ground-truth disagreement gate that falls back to the raw nearest camera lift a 15° gap from 22.3 dB to 29.2 dB against 24.8 dB for cutting (held-out seeds 29.2); with a bystander the gate loses its edge (26.1 vs 26.3 for plain filling). Toy scene.
Which platform can follow a creator through a crowd and keep the shot? A drone that ignores pedestrians frames 99.9% of the time but falls to 39% at 0.3 people/m² once it avoids them; a wheeled robot is stopped by step lines 42–47% of the walk, and a flat-floor one that ignores people passes within 0.5 m ~500 times an hour. 2-D simulation, assumed platform figures.
How much of a multi-camera shoot can an automatic edit recover? At detector noise 0.3 a fixed 3 s rotation shows mean true quality 0.546, a cut-cost (Viterbi) edit 0.802 vs 0.815 on true scores, and best-score-every-frame 0.723 at 345 cuts a minute; clock sync fails first on short clips (5 s at noise 0.25: 25% over 40 ms). Synthetic quality model, no real footage.
When does automatic blurring miss a bystander's face? On an assumed size-recall model a face detector leaves 5% of identifiable faces unblurred per frame, blurring the head of any detected body under 0.1%, and independent per-frame misses show a face in some frame of a 5 s shot 100% of the time; an offline whole-track blur leaves 0 to 5%. No real footage or detector.
Does recording only on a trigger save battery, and what does it miss? With 6 thirty-second moments an hour, standby with a 10 s pre-roll uses 19.4 Wh of an 80 Wh continuous day (76% less) and captures 90% of interesting seconds; deep sleep uses 7.7 Wh but captures 69%. Misses and wake latency, not the battery, set coverage. Assumed device figures, synthetic day.
When a camera rig records only on a trigger, should every camera have its own, or should one wake the rest? Four standby cameras with their own triggers use 80 Wh of 320 Wh continuous but get all four angles on only 68% of interesting seconds; one sentinel waking the others costs the same and gives 90.5%, and any-camera wake gives 100% for 92 Wh but its false-alarm energy grows with detector count. Assumed device figures.
Where in a camera ring should the sentinel go when the subject faces a favourite direction? A sentinel facing the favourite direction misses 8.6% of moments against 34.4% for the one behind; spread cameras' misses are anti-correlated, so capture-wake's independence assumption overstates the all-miss rate by 2x on a ring of 4 and understates it 12x for a tight cluster. With the turned-face miss measured in capture-detectors (54 faces) in place of the assumed curve, placement matters only if the back of a head goes undetected (untested), and weak detectors miss 8 to 45% of moments even with four cameras listening.
Does a longer window or a delay prior fix GCC sync's aliasing on real clips? Window length (shared audio) is the lever: 97% wrong at 1 s, 38% at 2 s, 16% at 3 s on the failing clips; a tone clip needs a prior tighter than its period.
How long a window of sound syncs two drifting cameras? GCC-PHAT plus a robust line fit syncs to under 0.02 ms over an hour from -10 dB SNR with 2 s windows; a sync made once at the start drifts one frame in 833 s at 40 ppm.
How small can a face be before a real detector misses it? YuNet found every face of 16 px or wider and half at 10 px (assumed: 20), cutting the modelled blur leak on an 8K 360 camera from 4.8% to 0.01%; YOLOX finds half of people at 23 px tall. A pilot on 22 easy faces in 128 COCO photos: an optimistic bound.
Does a predictive planner recover the framing a follow camera loses by avoiding pedestrians? Not at equal settings (drone 58% framed vs 68% for repulsion at 0.1 people/m²), but it halves-to-tenths the contacts (36 vs 161 per hour; wheeled 21 vs 326) and moves the framing/contacts front left. 2-D simulation, assumed platform figures.
How much of a predictive follow camera's contact reduction survives noisy, delayed pedestrian detections? Framing is unchanged (57-61%) but a drone's contacts rise from 36 per hour with exact data to 120 at 0.3 m noise and 0.25 s delay, and 373 at 1 m and 1 s (ignoring pedestrians: 523). 2-D simulation, swept noise, perfect association assumed.
What does it cost a travel filming kit to carry its footage backup? Counting storage costs 3 of 18 shots at 4 kg; the lightest kit reaching all 18 grows from 3,900 g to 4,125 g.
Can a small model trained on many random scenes pick the per-pixel blend weight better than a hand-set ramp? A one-hidden-layer network beats the best soft gate by 0.57 dB on 40 held-out scenes (all 40 ahead) and recovers 0.36 of the headroom to the best per-pixel blend.
Does the synthetic audio-sync threshold hold on real sound? No: on 10 real clips 2 s windows fail 53% of the time at -10 dB SNR (0% synthetic), and partial whitening instead of PHAT halves that.
Does an automatic multi-camera edit survive sync errors measured on real clips? Not as on synthetic audio: 34% of cuts jump over a frame at 0 dB SNR (64% at -10 dB) against none, depending on the clip; partial whitening cuts the 0 dB figure to 1.4%.
What does the capture-kit packing result look like with real, sourced devices (Insta360 X4, DJI Osmo Action 4, iPhone 15 Pro Max, Sony a7C II and lenses, Anker packs)? Exact search reaches all 18 shots at 4 kg, greedy stalls at 12; the unsourced mount masses move the exact figure by up to 10 shots.
Does a clip-free residual-from-the-clock-line trim beat the PSR gate? At 0 dB a little (1.4% to 0.9% of cuts over a frame); at -10 dB no (46% vs 38% for PSR).
In a reverberant room, does PHAT win after all? No: across 10 simulated rooms PHAT is the worst fixed weighting; gamma 0.5 cuts failures from 0.26 to 0.09, and choosing gamma per window by peak-to-sidelobe ratio helps less than just fixing it.
Does a soft confidence weight beat a hard switch for repairing stereo-depth view synthesis, and does the matcher's cost help? A ramped weight on warp disagreement beats the hard gate by 0.1 to 0.5 dB in every condition (29.5 vs 29.3 dB held out at 15°) and leaves a quarter fewer seams, closing only a tenth of the oracle gap; matching cost is a worse signal than disagreement (level with hole filling, worse with a bystander). Toy scene.
How much footage does a multi-camera travel kit produce, and what limits carrying and backing it up? Four cameras make ~860 GB a day; cards weigh ~8 g but the evening copy takes 2.7 h on one reader, so a safe plan needs 6 readers and ~450 g (assumed device figures).
How often must free-running cameras be re-synced by audio? At 40 ppm a sync lasts 1000 s for a 40 ms tolerance; a drift gate on fresh estimates helps only if you re-sync every 300 s. Synthetic audio.
Does a residual audio-sync error show at the cuts of an automatic edit? A sync made once leaves 50% of cuts jumping over a frame; a robust fit leaves none down to -10 dB SNR (2 s windows) and then fails outright, with 11 to 24% of cuts repeating or dropping a loud event.
Does a robust fit or a Kalman filter hold a camera clock better between audio re-syncs? On a clock rate computed from a sourced AT-cut crystal curve the plain offset hold is already fine up to 1800 s and every fit ties; only a Kalman filter tuned to an assumed 30 ppm wobble wins. Synthetic audio.
Does a coarse offset first let short windows sync drifting cameras? A 10 s window finds the offset, then 0.5 s windows hold within a frame from -12 dB SNR; plain 1 s windows fail to -5 dB. Synthetic audio.
Does a peak-sharpness gate plus settings chosen on other clips keep the edit in sync? At 0 dB yes (1.9% of cuts over a frame held-out vs 34% for PHAT); at -10 dB only partly (39% vs 64%).
Does holding a fitted clock slope between audio re-syncs help? At 40 ppm it cuts out-of-tolerance time from 44% to 3.7% at 1800 s intervals, but an assumed rate wobble makes a strict line gate lock out. Synthetic audio; also corrects capture-syncbudget.
Can a delay prior from a camera's own earlier windows replace the oracle? Not yet: 22.5% to 37% wrong on the failing clips against 0% for the oracle, and an early alias becomes an hour-long lock-in.
Does telling the blend model which of two sources is wrong help, or does it need to choose between them? New occlusion and cross-check features add 0.03 dB; a per-pixel source weight adds 0.47 dB (40 of 40 test configs), recovering 0.54 of the headroom to the best blend.
Getting more from cheap sensors: fusing cheap IMUs and cameras, computational imaging, and 3D models from real captures, with the error floors that correlated errors set. Topic page →
How many cheap gyros, fused, match one better gyro at equal cost? With independent errors the price ratio must beat k² (100 for a 10× quieter unit); shared error above 1/k² means no array size ties; unequal white/bias improvement makes the answer depend on integration time. Stylised.
Does a shared temperature coefficient put a floor under an array of cheap gyros? The shared part of the tempco does not average out: in the illustrative case a 3× better gyro can no longer be matched at any array size above a 0.2 °C/min ramp over 100 s; compensation quality, not array size, decides.
How many frames from a small sensor, merged, match one frame from a sensor with A× the pixel area? A shot-noise-limited burst needs A frames, a read-noise-limited one up to A² (formula and simulation agree); splitting the same total exposure never ties; registration blur and bracketed HDR are measured. Synthetic scenes only.
What does a moving subject do to a burst merge? A plain mean ghosts at every speed and gets worse as frames are added (30.5 dB at 8 frames, 25.0 at 48), median and sigma-clip do no better for a slow subject, and a reference-guided merge keeps improving and ties a 4×-area frame at about 6 frames at 0.1 dB cost when nothing moves. Synthetic scenes only.
Can aligning a moving subject rescue a burst merge instead of rejecting it? Inside the subject, yes (37.0 dB against 31.5 for reject-only and 32.8 for a 4×-area frame at 8 frames), but over the whole image rejecting is as good or better (31.7 against 31.8 dB), the aligner moves 10–31% of static pixels on noise, and the revealed-background ring stays 4 dB short of the large frame. Synthetic scenes only.
Can a burst of hand-shaken low-resolution frames recover detail that merging and upsampling cannot? At 2× in bright light a least-squares reconstruction reaches 29.5 dB at 16 frames against 24.0 for merge-and-upsample and 26.6 for merge-and-deblur, so 2.9 dB is sub-pixel information; it nearly vanishes in dim light and falls to nothing at about 0.27 px of shift error. Synthetic scenes only.
How many milliseconds of camera-to-gyro time offset double a fused attitude error, and can an alignment fit recover it? About 12–14 ms at 30 deg/s motion; the fit recovers it to ~1 ms with motion and fails on a still platform. Synthetic, single axis.
How much motion does a camera-to-gyro offset fit need, and what does clock skew do to a one-off calibration? A 20 ms offset needs about 16 deg/s rms motion to fit reliably; 1000 ppm skew leaves 0.254 deg error after a fixed-offset fit against 0.155 deg when skew is fitted too. Stylised, synthetic.
How accurate must a scan be to rebuild a part as parametric CAD? On synthetic plate scans, RANSAC plane and circle fits give all five dimensions within 0.2 mm for noise up to 0.2 mm, but at 0.5 mm noise the error is a bias (thickness −0.20 mm) that more points do not remove, and a 0.5% scale error alone moves an 80 mm length by 0.40 mm. Synthetic, one shape.
How many photos does a usable 3-D reconstruction need? On a synthetic object with known cameras, 12 views on a full orbit triangulate every feature, 8 views 89% and 4 or fewer at most 13%; per-point error then depends on pixel noise and pose error, not view count. Triangulation stage only (synthetic).
Does a low-resolution thermal camera find people in darkness and smoke, and what does misalignment cost? On synthetic scenes RGB finds 36% in bright light and none in the dark or dense smoke, thermal alone 65% everywhere (capped by warm decoys), fusion 94% in bright light and the thermal level otherwise; a 4 px (one thermal pixel) displacement costs the fused detector 19 points and 6 px erases the gain. Synthetic only.
Which upgrade buys the most visual-inertial accuracy, a sharper camera or a better IMU? On a planar synthetic smoother only camera resolution moved drift (1280 px 1.2 % vs 1.7 % at 640 px); a 0.25–4× change in IMU noise did not, on 12 s paths. Stylised, not EuRoC.
With 12 views, 0.5 px noise and every camera pose wrong, bundle adjustment cuts mean surface error from 0.0117 to 0.0014 object radii (the true-pose floor), 8× here and 73× at 0.2 radii of position error, but only 1.4× at 4 px of pixel noise and not at all with 4 views. Synthetic only
With 12 views, wrong poses and a focal length told 5% wrong, a fixed-focal adjustment costs 1.2× the true-focal error (2.7× at 20%); solving for the focal returns the floor with the focal within 0.3%, and for k1 = −0.3 distortion 0.0034 falls to 0.0015, but not at 4 views or above 2 px noise. Synthetic only
Rendering with k1 = −0.2 and k2 swept from −0.2 to +0.4, a bundle adjustment solving for the focal and k1 only returns 0.0015 object radii, the same as one that also solves k2, against 0.0022–0.0030 with no distortion model; the lens parameters are not separately identified (k1 stays near −0.16, k2 sits about 0.16 low) and the gain vanishes by 2 px noise. Synthetic only
Moving the camera in and shortening the focal length (800 to 400 px) raises the largest normalised radius from 0.34 to 0.85, and the spread of the fitted k2 over seeds falls from 0.33 to 0.02 with its mean within 0.01 of truth; the surface then needs k2 (0.0027 with k1 only against 0.0020 with both). Synthetic only
With 12 views and wrong camera poses, 2% of observations replaced by random pixels already raise bundle-adjustment surface error from 0.0014 to 0.079 object radii, and Huber or Cauchy loss from the usual all-view start only halve that; a per-point RANSAC start fixes 5% (0.0319) but only 24 views get back to the clean floor at 10% (0.0012). Synthetic only
A 10 px principal-point offset held at the image centre raises the surface error from 0.0019 to 0.0043 object radii on the wide rig (focal 3.5% off) against 0.0019 to 0.0015 fitted on the narrow one; fitting the point recovers it and removes the cost. Synthetic only
Inverting the burst break-even formula: the largest sensor-area ratio a K-frame burst matches runs from √K in the dark to K in bright light, so 8 frames at 3 e⁻ read noise match a 4×-area frame from 4.5 e⁻ per pixel per frame, a 6× frame from 21 e⁻ and never an 8× frame; Monte Carlo agrees to 1% in variance at 18 settings. Model only, swept ranges not sourced to a device
On OpenCV's 13 real checkerboard photos, random subsets of 3 views put the focal length within 2% of the 13-view value in 99% of draws (5–95% band 2.3% wide), 12 views give 0.5%; noise-only re-renders predict the band, and a one-term lens model doubles held-out error. One camera, one board
An epipolar gate removes 93% of 10% random-pixel mismatches (5% of good observations lost) and takes 5% contamination from 0.168 to 0.0061 object radii, but a RANSAC start does as well at 10% and better at 20%; near-miss mismatches are mild for a robust loss already. Synthetic only
When a bad feature is wrong by the same offset in more consecutive views, the gate's recall falls from 0.81 to 0.59 at a 10% wrong rate and its lead over a RANSAC start shrinks from 1.7x to a tie within seed noise, though typical errors stay at 2 to 3.5 times the clean floor; a single failed seed in 12 can dominate a mean
With the mismatch rates and mixes measured from SIFT on a real stereo pair, a ratio test of 0.8 to 0.6 (10% to 5% wrong) leaves gate + Cauchy adjustment at 0.008 to 0.003 object radii against 0.013 to 0.004 for the RANSAC start, and the all-random-pixel assumption overstated plain Cauchy's error 1.3 to 59 times; with no ratio test (56% wrong) every method fails
Does modelling the sub-pixel coverage of a moving subject fix the edge ring? Yes, on a known shape: a layered disc-over-background model fitted from the burst lifts the ring from 27.1 to 33.1 dB at 8 frames and 2 px per frame (4×-area frame: 31.7 dB), less at slow speeds, and it is sensitive to a 0.5 px centre error. Synthetic flat disc only.
Can a temporal-median background or a subject mask fix the edge ring that burst alignment leaves behind? No: four ring treatments leave it at 21.6–27.2 dB at 8 frames against 31.6–32.0 for a 4×-area frame, none beats plain aligned-plus-reject (27.0 dB), and the mask misses most of a slow subject. Synthetic scenes only.
On 30 warped real photographs SIFT keypoints localise to 0.13 px per axis at zero noise and 0.32 px at noise sigma 10 grey levels, 0.59 px at 40, so sensing-ba's assumed 0.5 px sits at roughly sigma 28; large keypoints are worse, blur matters little
With the mismatch rates and along/near/far mixes measured for SIFT, a ratio test of 0.8 or tighter (10% wrong or fewer) leaves gate and RANSAC-start adjustment near the clean floor (0.002 to 0.02 radii) while an all-view start is 0.005 to 0.39; at ratio 0.9 the RANSAC start wins and with no ratio test (56% wrong) everything fails. Synthetic rig, measured mixes
On a real Middlebury stereo pair SIFT with no ratio test is 56% wrong and 84% of the wrong ones are far, but at a 0.7 ratio test 6% are wrong and 62% of those lie on the true epipolar line (chance: 1%); ten warped photographs give 40% wrong without and 2% with ratio 0.6
Feeding sensing-matchreal's measured SIFT mismatch mixes into the sensing-epigate trial, gate plus Cauchy beats a RANSAC start at ratio tests of 0.8 and tighter (0.0078 against 0.0207 object radii at 0.8) and loses only at a loose 0.9 ratio test, where all methods exceed 0.08; synthetic geometry, 6 seeds
With a 1/f accelerometer bias, a filter with no bias state claims 2.9 m after a 300 s GNSS outage when the RMS is 151 m (NEES/dof 514 to 2,000 at 100 ug); a random walk read off the Allan curve at 1 s or 10 s claims 2.4 to 3.7 times the true error, and at 100 s close to honest (0.9 to 1.6). Synthetic bias, swept instability
A Schur-complement prior in the sensing-vio planar smoother cuts rms drift on 30 s paths from 12.3 % to 2.5 % of path (8 seeds, baseline IMU), and IMU grade then orders the results (0.25x noise 2.1 %, 1x 2.5 %, 4x 6.5 %), unlike with the pinned prior; planar and synthetic, not EuRoC
How densely, cheaply and durably energy can be stored, and what mix of supply and storage meets demand at least cost: the physical limits first, then devices, costs and grids, in open code. Topic page →
How big should a home's solar array and battery be, and at what price does the battery pay? Hourly model on synthetic weather (assumed inputs): a 6 kW array meets 35% of an 8,000 kWh/yr load, a 10 kWh battery lifts it to 59%, and the battery pays only below about $451/kWh installed at $0.05 export (assumed price $800).
Does time-of-use pricing make a home battery pay, and which size? On an assumed tariff with the flat tariff's average, a 10 kWh battery behind 6 kW PV breaks even at $641/kWh installed against $444 flat (assumed price $800); only 2.5 to 5 kWh clears $800, and the peak price steers the answer (energy-home with hourly prices).
What is the cheapest mix of solar, wind, gas and storage that cuts emissions, and what does the last 5% cost? PyPSA on 2019 German hourly demand (assumed costs): $79/MWh all-gas, $113 at an 80% cut, $177 at zero emissions with 10.6 TWh of hydrogen storage; abatement cost $30/t to $1,765/t for the last 5%. Stylised.
How much energy can each storage technology hold per kilogram, at the most? First-principles ceilings that reproduce five published values within 0.3% (Li-S 2,567, Li-O2 3,458 Wh/kg). No battery couple exceeds 1.65 eV per reactant atom, so light atoms set the winners (Wh/kg = 26,801 × eV/atom ÷ g/mol); flywheels top out near 0.3 eV/atom, heat and pumped hydro far lower. Active material only. First project of track 16.
How much energy can each storage chemistry hold per litre, and does the ranking by weight survive? Volumetric ceilings from reactant densities: zinc-air 9,659 Wh/L with air, Li-ion 1,382, lead-acid 724, hydrogen 1,314 at 700 bar.
How close do real batteries, flow cells and hydrogen tanks get to their first-principles ceilings? A Panasonic NCR18650B cell reaches 0.64 of the Li-ion reactant ceiling (243 of 380 Wh/kg), LiFePO4 0.25–0.45, lead-acid 0.21–0.24; DOE's projected 700 bar H2 system is 5.1% hydrogen by mass against 24–41% ideal. Small sourced dataset, primary and secondary rows marked. Second project of track 16.
Can a house-sized sand heat store carry summer heat into winter? A transient model: 10 MWh after 120 days needs 222 m³ (70 if lossless) and returns 26% of the electricity as heat, so a COP-4 heat pump wins unless its electricity is 15× dearer; a days-scale store at house size. Stylised.
Which storage technology is cheapest per MWh delivered, by duration? Li-ion wins to about 4 h ($116/MWh), cavern stores beyond ($109 vs Li-ion $337 at 24 h), cavern hydrogen only past ~300 h. All inputs assumed. Stylised.
How much better can a Li-ion cell get by redesigning its electrodes, and does a smarter search help? In a PyBaMM model, thicker, more porous electrodes with more negative capacity lift energy after 100 cycles from 109 to ~143 Wh/kg (+30%); random, Bayesian and session-agent proposers end within 3% of each other. One aggressively ageing parameter set. Stylised.
How robust is the cheapest storage technology by duration to uncertain costs? Monte Carlo over energy-lcos: Li-ion wins 96% of scenarios at 2 h but 18% at 8 h; no technology wins over 48% between 6 and 12 h; caverns win most from 24 h. Ranges assumed. Stylised.
Re-scoring 49 designs from energy-cell under PyBaMM's full DFN model instead of SPMe: rank correlation 0.86 at cycle 100, the SPMe winner is 3rd of 45 and still +38% over the reference cell (+31% under SPMe), DFN reports about 19 Wh/kg more on average, and SPMe fails to cycle 3 designs DFN handles (modelled, stack level)
How hard does a least-cost zero-emission German grid cycle its storage? Batteries about 1,700–1,900 h a year (near the assumed 2,000), cavern hydrogen only 719 h, which more than doubles its LCOS to $864/MWh.
Which storage technology is cheapest at each duration once costs are sourced (NREL ATB 2024, PyPSA technology-data)? Li-ion to 4 h, cavern compressed air from 6 h; at 8 h pumped hydro 52%, air 27%, Li-ion 22% of scenarios; hydrogen's assumed 500 h win does not survive.
What does a zero-emission German power system cost once energy-mix's assumed costs are replaced by sourced ones? PyPSA on 2019 hourly demand with PyPSA technology-data costs (Danish Energy Agency et al.): EUR 222/MWh with a steel hydrogen tank, EUR 144 with caverns, EUR 75 unconstrained; the storage type moves the answer more than the cost year.
Which weather year sets the hydrogen store of a zero-emission German power system? The same sourced-cost PyPSA model on 2015 to 2019: EUR 203 to 271/MWh with a steel tank, EUR 141 to 155 with caverns, and a cavern store of 24 to 36 TWh depending on the year.
Does residual load explain German day-ahead prices on a year the model never saw? Yes: correlation 0.87 and RMSE 9.6 EUR/MWh on 2019 against 23.0 for the flat merit-order price; the cheap-quarter mean is within EUR 4–9/MWh; the rest is the fuel-price level.
Does a weather-dependent heat-pump COP change the sand-store verdict? The table's 3.6 equals a 35 C floor-heating sink; at 45 to 55 C the store's weekly flip multiplier rises 8 to 46%, and 2018 still favours the pump.
How far must capex move to flip the sand-store vs heat-pump verdict? Weekly cycling flips on a 2 to 40% store-capex change (the cost table's own vintage step is 26%); daily cycling holds to 2 to 3.5 times.
How much can the sand store's heat exchanger cost? Weekly cycling survives about 120 to 270 EUR per kW in four of five price years; daily cycling survives 460 to 900; 2018 never wins.
Does the sand-store vs heat-pump verdict survive a modelled price? Mostly: 32 of 40 cells agree with real prices (21 for the flat merit-order price), but weekly cycling, whose margin is under EUR 0.011/kWh, is wrong in sign in 5 of 5 years; as a charge scheduler the model costs under EUR 0.0011/kWh.
How much cheaper must electricity be for a sand heat store to beat a heat pump? Sourced costs (PyPSA technology-data) on the energy-thermal model: a daily-cycled store needs the pump's electricity about 2 times dearer, weekly 5, monthly 16, seasonal 120 (house); the heat lost in standby, not the sand, rules out seasonal storage.
When does a sand heat store beat a heat pump on hourly prices? With 189 GW solar and 137 GW wind and a modelled German price series, a daily or weekly store wins in all 5 years (EUR 0.027/kWh against 0.071); a levy of 0.10/kWh or a surplus-hour price above about 20–35 EUR/MWh removes the win.
On real German day-ahead prices, does a sand heat store beat a heat pump? Yes at wholesale: daily cycling wins in all 5 years (EUR 0.045–0.062/kWh against 0.070–0.074) and weekly in 4; the earlier merit-order model was flat at EUR 54.6/MWh and wrong; a EUR 0.10/kWh levy removes the win.
How much is a home battery worth on a time-of-use tariff with optimal dispatch? An LP breaks even at $867/kWh for 10 kWh behind 6 kW PV, against $674 for the best fixed rule ($742 with a 4,000-cycle life); a rolling 36 h plan matches the year optimum (energy-tou with an optimiser).
How much of an optimal home-battery controller's gain survives a realistic forecast? With yesterday's weather or a 7-day mean as the forecast, a rolling LP saves $726 or $691 a year against the fixed rule's $694 (perfect forecast: $892); 84–101% of the gain is lost (energy-tou-lp with forecasts).
How much of the home-battery optimiser's forecast loss does re-planning every few hours recover? On PVGIS typical-year data for three US sites, re-planning the LP every 3–12 h instead of daily adds $10–36 a year and closes at most 17 points of the gap to a perfect forecast (10 kWh, assumed tariff); energy-tou-lp-tmy with receding-horizon re-planning.
Does a clear-sky-index forecast rescue the optimal home-battery controller on real weather? On PVGIS typical-year data for three US sites, a rolling LP fed yesterday's weather or a clear-sky-index forecast keeps 25–55% of the perfect-forecast gain over the fixed rule at Phoenix and Seattle and none of it at Golden (10 kWh, assumed tariff); energy-tou-lp-forecast on measured-derived irradiance.
DC against AC optimal power flow in pandapower on the IEEE 30-, 39- and 118-bus cases: the DC model's cost is 1 to 3 % below the AC optimum (it ignores losses); on the 118-bus case its dispatch is feasible but costs 0.7 to 1.7 % more than the AC optimum once losses are paid, and on the 39-bus case it breaks voltage limits (15 buses at 0.6 of load) at almost no cost difference (modelled benchmark, not a measured system; tightened-limit runs often had no solution). Feeding the AC losses back into the DC model (a loss-adjusted DC) brings the 118-bus cost estimate to within 0.6 to 1.2 % of the AC optimum, but repairs only 13 to 32 % of the dispatch's excess cost and none of case39's voltage violations.
Ball-mill population balance (Austin form): at the same 100 um P80 a closed circuit at 278% circulating load uses 0.47 of the open-circuit energy, 1.8 to 3.7 times better across the swept mill and classifier inputs, far above Bond's 1.2 open-circuit factor and a vendor's ~10% for cement; the model's size exponent matches Bond's only at a selection exponent near 0.5.
Stochastic PV hosting capacity of the IEEE 13-node feeder in OpenDSS on 300 random placements: median 1,015 kW at midday minimum load, voltage binds first in 75% of placements; a 2 V lower regulator set-point adds +310 kW, while inverter fixed power factor and volt-var add about nothing once the regulators respond (modelled, not a measured feeder).
PV hosting capacity of the IEEE 34- and 123-node feeders in OpenDSS (200 random placements): on the 123-node feeder a 2 V lower regulator set-point adds +790 kW to a 1,160 kW median (every placement better), inverter volt-var +100 kW and fixed power factor +180 kW; the published 34-node case has no headroom at all because its source is set to 1.05 pu (modelled, not measured feeders); over a one-minute day the set-point trades overvoltage for undervoltage while inverter reactive power cuts tap operations about 30 %.
Does MPC beat a thermostat for a heat pump on a time-of-use tariff? On real TMY3 weather with a deliberately wrong model and yesterday's weather as the forecast it pays 10.7% less in Greensboro (4.1% in cold Sand Point), saves more with more thermal mass (6.5% to 25%), and loses the gain at an 8 K forecast error; the envelope is from published values, not a fit to measured data.
DC against AC N-1 screening on IEEE 14-, 30-, 39-, 57- and 118-bus cases (every line and transformer outage, modelled, ratings swept): at 25 % rating headroom the DC screen misses 13 to 40 % of the outages an AC power flow calls insecure; flagging at 0.8 of rating misses none, at the cost of 102 false alarms on case118 (186 outages).
Nodal loss penalty factors (AC loss sensitivities) in a DC OPF on the IEEE 30-, 39- and 118-bus cases: on the 118-bus case they recover 23 to 38 % of plain DC's excess cost at 0.6 to 1.0 of load, but the iteration does not converge at 0.8 and above and at 1.1 of load the dispatch is worse than plain DC (modelled benchmark, not a measured system).
Freight energy per tonne-km from first principles for truck, unit train, bulk carrier and 747 freighter, then diesel swapped for batteries or hydrogen at the same gross mass and range: at 250 Wh/kg a truck keeps 79% of its payload, a train 93%, a ship 55% and the freighter cannot fly the route; 90% needs ~510, 180, 990 and 5,600 Wh/kg (most inputs assumed and swept).
Net3 pump schedules billed on PG&E B-19 over a month of varying days: with every day the same the best schedule saves 56 to 67 %, but the lowest feasible peak jumps from 63 kW to the 310 kW booster at only 1.5 % more demand, and one day at +20 % cuts the saving to 44 % (summer) and 19 % (winter, spring) (simulated; one network, list prices).
Net3 pump scheduling billed on PG&E's published B-19 tariff with demand charges at a 15-minute step: the lake-pump schedules that idle the 310 kW booster cut the monthly bill 56 to 67 % (peak 373 to 63 kW), and the demand charge, 60 to 64 % of the shipped bill, does not move the optimal schedule at any size from 0 to 20 times (simulated; one network, list prices).
Pump scheduling on EPANET's Net3 (WNTR): running the lake pump 21 h from 01:00 cuts pumping energy 52 % at a flat tariff because it idles the booster pump; the time-of-use tariff adds 3 to 16 % of cost at a ratio of 3 or less, and hourly on/off schedules (21,806 simulated, plus a GA) add almost nothing beyond one window once tank drawdown is priced (simulated, assumed tariff shapes).
Distribution transformer ageing under heat-pump and EV growth: an IEEE C57.91-form thermal model on TMY weather and a standard load profile; loss of life stays under 0.01%/yr until ~50% of homes electrify, then 5.6%/yr at 100% with uncoordinated charging against 1.07%/yr with valley-filled charging (constants swept, not verified).
Simulated societies of AI-driven robots living among simulated people: the conventions that emerge, who sets them, what they cost people, and watchable episodes made from seeded runs. Topic page →
How many robots does it take to change which side a crowd walks on? Robots that hold a programmed side tip a crowd once they are 16–32% of it, more when people remember more past partners (simulation matches mean field within 0.02); just short of that they make people collide up to 14× as often as adaptive robots, and placement matters more than numbers when people meet only neighbours. Stylised.
Do robots that keep to one side make people walk on it, or jam the corridor? In a social-force corridor, robots that adapt change nothing, but robots that hold the left cut people's speed from 0.91 to 0.39 of desired by 30% of the crowd and halve lane separation, while people move to their side only gradually (no sharp tipping, unlike the 1D model). Stylised.
Can a robot fleet's reputation survive one bad incident? In a model where trust spreads by experience and gossip, a dent always recovers because people keep meeting robots; reputation is lost only through avoidance (at a 0.30 avoid-below threshold, 20/20, 18/20 and 0/20 crowds recover under neutral, 2× and 4× negativity in gossip), and robots that explain failures recovered every time. Stylised.
What does it cost robots to let people go first at a shared lift or narrow pavement? At load 0.9, deference cuts people's wait 6.5× (4.60 to 0.71) and raises robots' by 2.6 units; total waiting cost is conserved, so it pays only if a person's wait costs more than a robot's, and a lone defector waits far less (2.08 vs 7.65). Queueing model within 2.7% of closed forms.
Do robot agents keep the norms they state? A pluggable town harness with a deterministic stub (no language model run): a robot stating "always yield" keeps it in 1 − 0.4×pressure of meetings (1.00 to 0.60), and people's cost per meeting rises from 0.20 to 1.08. Stylised.
Does the robots-in-a-corridor conclusion survive a more humanlike crowd? Adaptive robots stay free and committed robots never flip the crowd in all five simulated crowds, but the size of the slowdown (loss of 0.17–0.49 of desired speed at 30% robots) and of personal-space intrusions (0.03–0.36 of agent time) depends strongly on how humanlike the people are. Stylised.
How many robots does it take to change a crowd's walking side when some people never adapt? With 0, 20, 40 and 50% stubborn walkers the mean-field tipping share (memory 9) rises 0.217, 0.240, 0.283, 0.329, simulation agrees within 0.02, and committed-robot conflict costs barely change. Stylised.
How many robots does it take to change a crowd's walking side when some people always walk on the robots' side? Each 5% of always-robot-side people cuts the memory-9 mean-field tipping share (0.217) by about 0.04, 25% tip a crowd with no robots, opposing blocs raise the bar, and simulation agrees within 0.01. Stylised.
Does a stubborn block that slowly converts let a smaller robot minority tip a crowd's walking side? With 40% stubborn walkers, 24% robots never tip (0 of 12) but tip all 12 at 0.1% conversion per round (median round 721).
Can a simulation run be turned into a watchable, honest episode? Five seeded, labelled-fiction episodes of a robot town built on society-trust, with turning points found by code and a narration read from the record: even-handed gossip recovers, 4× negativity locks the town out, explained failures recover, and 2× ends both ways by seed. Stylised.
On a ring where people meet partners within 2 sites (memory 9), evenly spread robots at 12% tip every crowd but blocks of 3 or more tip none; at 20% blocks up to 3 still tip, and the largest tipping block grows with the neighbourhood (2 at k = 1 or 2, 4 at k = 3 or 5, 8 at k = 10).
How fast can a bloc on the robots' side dissolve? With 20% allies converting at rate c per round, the least grid robot share that tips half of 12 crowds rises from 0.02 (no fading) to 0.05, 0.10, 0.10, 0.15 and 0.20 at c = 0.001 to 0.1; tips form in about 50 rounds and persist once allies are gone. Stylised
Allies who fade by the share of R among only their last k partners (k = 1, 3, 5, 9) tip about as many crowds as the whole-memory rule: at c = 0.01 and robots 0.10, 11 to 12 of 12 against 10 for constant fading; at c = 0.03, robots 0.15, 12 of 12 against 10. Differences between k are one crowd of 12. Stylised
Allies who convert only when they have watched the crowd walk the other way. With 20% allies, fading at rate c times the share of R in their memory tips more crowds than a constant rate c once robots are 0.10 or more (12/12 vs 10/12 at c = 0.01, robots 0.10; 4/12 vs 0/12 at c = 0.03), but does nothing below 0.05. Stylised
How much cheaper must an urgency cue be for the urgent before a door robot can rely on it? Urgent people must pay at most about half what normal people do; the crowd is worse off than under yield-all in every cell.
At what collision cost does a door stop tempting robots to go first? With 30% robots and dithering cost 1, always-yielding robots are individually stable only above a collision cost of 2.80 (waiting cost 1); below it a single robot gains by going though yielding is best for the crowd. The threshold rises with dithering cost and robot share.
When robots always yield at a door, do people learn to walk through first, and who pays? Always-yielding robots raise the share of people who go from 0.388 to 0.595 at 50% robots and cut the crowd's cost (1.064 to 0.968); always-going robots raise it to 1.373. Mean field and simulation agree within 0.003.
How many enforcer robots hold a queue against line-cutting robots? About 5% of the crowd holds the norm against 30% cutters (memory 9, 10 people in view of each cut, stop chance 0.5), simulation agrees. Stylised: view size and stop chance are swept, not sourced.
Do stubborn walkers who convert after meeting robots let a smaller robot minority tip a crowd's walking side? At 24% robots every crowd tips for k = 30 meetings (median round 171) though the fixed block stops it; at 16-20% none tip.
Can a robot that yields to people in a hurry survive people faking a hurry? With 30% robots, no signal cost on a 0 to 1.2 grid lets a signal-reading fleet beat yield-all for the crowd, and urgent people keep about 6% of the gain they get from perfect reading.
On a 16x16 torus (memory 9), robot patches up to about 2k+1 sites wide tip every crowd at robot share 0.25 and wider ones tip few or none; one 8x8 patch of all the robots tips none at any neighbourhood radius up to 5.
Is a hand-over cheaper than buying robots first? With 20% allies fading at rate c and 10% robots at the start, replacing half of fading allies with robots tips 10 of 12 crowds at c = 0.03 but ends with 0.19 robots, against 0.15 robots upfront in society-allyfade; below 5% initial robots only full replacement tips anything. Stylised
Do door robots that learn from their own costs keep honouring an urgency cue? They keep yielding to cue senders but stop going against everyone else, which erases most of the cue's gain to urgent people.
Do robots that learn at a door drift to going first when collisions are cheap? No: with 30% robots they settle on a mix whose go share falls smoothly with collision cost (0.51 at k = 1.5, 0.03 at k = 2.8), whatever they start from, at a higher crowd cost than a fixed yielding fleet for k of 1 or more.
How many line-cutting robots break a queueing norm? Mean-field critical share 12.7% (memory 9, lone-cut objection 0.9), simulation agrees; depends mostly on how fast objection fades. Stylised: objection strength is swept, not sourced.
Do real objection rates keep a queue norm? People alone need to stop a lone cut at least 0.786 of the time; Milgram's field reactions (about 0.5, secondary source) imply 7.5% enforcer robots even with no cutters. Inputs not read from the paper; p0 is swept.
Does a signal-reading door fleet help people once robots are not counted? Only if the urgent cue costs them about a third of what it costs others, or a planner weights urgent waiting; an equal-cost cue hurts people at every weight tried.
A deterministic local mean-field agrees with the society-allies simulation on tip/no-tip in 145 of 160 cells and is almost never too optimistic, but it overstates the share of evenly spread robots needed (0.20 against 0.12 at k = 2).
Neither alone: a noisy memoryless map tips at 0.06 robot share for spread robots, the simulation at 0.10 and the deterministic mean-field at 0.18 (k = 2).
Fitting the stubborn-bloc model to the side preference Moussaïd et al. (2009) measured for two head-on walkers (about 17.5% left, read from their Fig. 4) puts the mean-field tipping robot share at 0.075 to 0.096 for memory 9 across error rates 0.02 to 0.30, against 0.217 for an unbiased crowd; memory matters more (0.033 to 0.053 at 5, 0.133 to 0.149 at 17) and a stubborn-right bloc raises it.
Should a robot yield only to people in a hurry, or to everyone? With 30% robots and 20% urgent people, a fleet that yields only to the urgent cuts their cost by 40% (1.130 to 0.676) at a 3% cost to everyone else, is individually stable, and costs the robots 29%.
Designing a cheap robot and its controller together in simulation, with an agent, CMA-ES, Bayesian optimisation and random search at equal budget, for civilian domains. Topic page →
Which printable two-finger gripper holds eight objects for the least plastic, and can an agent beat CMA-ES and Bayesian optimisation at 40 MuJoCo evaluations? Median best objective 0.991 (Bayesian opt) vs 0.979 (CMA-ES), 0.965 (random) and 0.963 (session agent, one run); the cheapest winners (0.5 g flat fingers) are also the most fragile when object offsets triple. Stylised, no learned policy.
Which cheap wheel-legged rover covers the most stylised rubble under a 120 USD cap, and can an agent beat CMA-ES and Bayesian optimisation at 40 evaluations? Wheel radius at its bound plus about 0.5 N m torque reaches the ceiling (J 0.783, 69 USD); Bayesian opt and CMA-ES 0.782, session agent 0.783, random 0.716; stylised, falls never occurred.
Which three-finger pad design picks the most unbruised strawberry-like fruit under a 60 USD cap, and can an agent beat CMA-ES and Bayesian optimisation at 40 evaluations? Bayesian optimisation did (median J 0.635 against the agent's 0.618); about 20% of fruit are lost to clutter collisions no pad setting changes. Stylised, assumed constants.
Which suction gripper picks the most of a stylised mixed tote (boxes, polybags, bottles) under an 80 USD cap, and can an agent beat CMA-ES and Bayesian optimisation at 40 evaluations? The agent's best J was 0.519 against 0.478 for Bayesian optimisation (median of 20 seeds); the best design is two 18.5 mm cups at 80 kPa and 60 L/min, and a catalogue-default single 30 mm cup scores 0.075. Stylised, assumed constants.
Should a quadrotor's airframe and its learned roll controller be sized together? Yes in this stylised model: joint CMA-ES reaches 5.25° RMS roll error, equal to the grid optimum, against 7.06° for lightest-airframe-first; a controller reused across airframes is worse on 41% of them.
Does the best quadrotor airframe stay best under widened motor-strength, mass and lag randomisation? Mostly: top five unchanged (Spearman 0.75), but retuning gains helps the median airframe 0.91° (stylised).
Should airframe and gains be searched jointly under an uncertain plant? Yes in this stylised model: joint CMA-ES at 960 evaluations (5.75° median held-out, 8 seeds) beats random search and a 4800-evaluation grid-then-tune best cell (6.00°).
Is the airframe ranking from one tuning run reproducible? With wide-tuned gains yes (Spearman 0.99 over six replicates); with nominal-tuned gains it is noisier (0.84) and the earlier 0.17° regret was within noise (stylised).
Does the ranking of soft-fruit gripper designs survive a shift in friction, fruit, placement error and print tolerance? Yes in this model (Spearman 0.993 over 600 designs), but the nominal optimum loses 13% of its J and a robust optimum gains only about 0.015 on average; sim-to-sim, assumed ranges.
Which grasp scenes can no printable two-finger gripper hold? 10 of 140 (7%), all spheres with the hand more than about 2 mm above their centre height; lowering only the hand holds all 10, so the 0.85 plateau in codesign-diagnose is scene geometry, not friction or force (stylised, found after the fact, one intervention).
Does a failure summary or full rollout logs help a gripper design loop beyond the score alone? No: three scripted readers end at 0.84 to 0.86 best test success, like random search, CMA-ES and Bayesian optimisation (stylised, rule-based readers, not an LLM).
Do agent-proposed gripper fingers beat random search, CMA-ES and Bayesian optimisation when each design gets its own trained grasp force? On 40 held-out scenes all methods' best seeds reach 0.93 to 0.95 and the ranking is within noise; on 100 fresh scenes the session agent's 0.95 falls to 0.81, level with the baseline median (stylised, preliminary, mostly negative).
Does a rotor cant angle, co-designed with arm length and propeller size, beat the yaw limit that control-law changes could not move? In simulation yes: joint co-design with free cant (chosen at the 35° bound in 5 of 5 seeds) cuts held-out attitude error from 15.22° to 12.32°, at equal evaluations.
Does more rotor tilt keep helping once the 35° cap of codesign-aero-cant is lifted? In simulation no: with the bound at 35°, 50°, 65° and 80° the joint co-design reaches 12.3° held-out attitude error and picks 34–40° each time, so the optimum is interior and flat; an assumed tilt efficiency loss changes it by 0.1°.
Does the interior cant optimum survive a reaction torque that grows with propeller diameter (κ = c·D) instead of a fixed 0.016 m? In simulation yes: for c = 0.06, 0.126 and 0.25 the joint co-design reaches 12.5°, 12.3° and 11.8° held-out attitude error with the bound at 80°, picks 33–41° each time, and cant still beats no cant in 5 of 5 seeds; the gain is largest (−4.8°) for the weakest reaction torque.
Once the vehicle must hold position, does a canted-rotor quadrotor still win? In simulation cant still buys yaw (−6° RMS, 5 of 5 seeds) but not position, and the sideways force a tilted rotor makes under roll/pitch torque breaks designs tuned without it (1.1 m against 0.25 m position error).
What is the reaction-torque-to-thrust ratio of real small propellers, and does the best cant angle survive it? Measured static data for 77 propellers of 3.15–9.85 in give c = CP/(2π·CT) = 0.065–0.13 (median 0.081); in simulation cant still beats no cant in 5 of 5 seeds at every c, by 2.9–4.7°, and the joint design picks 36–41°.
Does rotor cant still help once motor headroom is a design variable? With thrust-to-weight free in 1.5–4 (no cant picks the 4.0 ceiling), cant to 35° still beats no cant in 5 of 5 seeds at each of three measured propeller c values, by 1.6–3.4°; headroom alone recovers 2.5–3.5° of the 3.8–4.7° the parent credited to cant.
Does raising the TWR ceiling from 4 to 6 and 8 erase the cant advantage? No: cant to 35° still beats no cant in 5 of 5 seeds at three measured propeller c values, by 1.5–3.0° at ceiling 8 (1.6–3.4° at 4); the optimiser stops near TWR 5 without cant.
Does a residual network or analytic gyroscopic compensation beat per-axis PID on a coupled three-axis quadrotor? No: the residual is worse than PID in 26 of 30 pairs (+0.32° held out) and compensation changes the error by 0.001°; yaw authority sets the error.
Does a 31-parameter neural roll controller beat the three-gain PID on a randomised quadrotor? Not at equal evaluations (7.7° PID against 9.0°); with 10× the evaluations it only matches it (7.6°), and the airframe ranking is unchanged (Spearman 1.00).
Does a zero-initialised neural residual on the tuned PID beat the PID on a randomised quadrotor? No at equal evaluations (7.68° against 7.58°, better in 7 of 18 pairs); the airframe ranking is unchanged (Spearman 1.00).
Does the strawberry-gripper co-design of codesign-agri survive measured stem pull-off forces (3.17 N bending and pulling, 13.94 N pulling alone) instead of an assumed 3.5 N? Partly: the optimiser ranking holds in 8 of 10 cells, but the best achievable objective falls from 0.665 to 0.075 as the median pull-off rises from 3.17 to 13.94 N, and at 13.94 N no 40-evaluation run finds a gripper that picks anything
Does the optimiser ranking of codesign-agri survive a sweep of its 12 invented constants? Mostly: Bayesian optimisation beats CMA-ES beats random search in 82 of 100 worlds, but the best gripper has 2, 3 or 4 fingers depending on stem strength and the nominal winner loses 0.06 J or goes over budget in most worlds
Does diagnostic feedback help a gripper design loop once the scene generator is fixed? Still no: every method gains only 0.00 to 0.05 (best test success 0.85 to 0.90) and the failure-summary and rollout-log readers do not beat random search, CMA-ES or Bayesian optimisation (stylised, rule-based readers, not an LLM).
Does the ranking of co-design methods survive 600 test scenes? No: re-scoring the 144 final designs of codesign-headroom gives 0.82 to 0.85 true success for every method, random search ties CMA-ES and Bayesian optimisation, and the rollout-log reader trails by 0.03 (interval includes 0)
Do more seeds separate the gripper co-design methods? Not yet: with 24 runs per method CMA-ES leads random search by 0.025 (interval -0.007 to +0.056), the rollout-log reader trails by 0.022, and a 0.02 gap would need about 140 runs per method
A robot that takes clothes from a dryer or a loader and hangs every item, with hangers designed in a simulation feedback loop: drape models, hanger shapes, hang-or-fold decisions and the robot cell. Topic page →
What hanger shape keeps a shirt in shape, and can one hanger fit every size for a laundry-hanging robot? In a 2D cloth-drape simulation the best single fixed hanger leaves garments 2.1 cm RMS from their worn shape (5.4 cm for a child's tee), one adjustable-width hanger set per garment 0.18 cm, and a rack of four widths under 1 cm for every size; thin wire ends fold the cloth at the tip. Stylised.
Should a laundry robot hang a garment or fold it, and what can it sense to tell? A stretch-set and crease-set model on five fabric archetypes: woven shirts and linen are better hung, tees, fleece and heavy knits better folded; shoulder width, mass and stretch when lifted pick the better action for 89–91% of 600 simulated garments (always fold: 59%). The split depends mostly on the assumed crease model. Stylised, assumed fabric constants.
How does a laundry robot get a hanger into a garment, and what does it cost the neck? A swept-section model of a rigid, telescoping or folding hanger passing a neck or hem loop: rigid hangers need 43–61 cm of loop, a tee's neck stretches up to 33% and a buttoned shirt collar cannot take them at all (shirts go in at the hem, 10 s against 6 s); a hanger that collapses to a 10 cm half width needs 31 cm. The round end hanger-fit wants costs about 3 cm more. Stylised, assumed constants.
How many dryers can one laundry-hanging robot serve, and what limits it? A discrete-event model of the whole cell (pick, sense, feeder, insertion, rail, fold table) fed by hanger-insert and hanger-fold: with assumed times one arm clears a 25-item load in 8.9 min (about 5 dryers), a second arm adds 22% before the fold table binds, and the five hanger designs differ by at most 3%; pick and fold times dominate. Stylised, assumed station times.
Can the hanger a cloth simulation designed be 3D-printed, and does it hold a garment? hanger-fit's adjustable shape and four-width rack as parametric STL and OpenSCAD with a beam check: the round-ended arm has a safety factor of 40–70 in assumed PLA, a wire-like arm 0.13, and no useful width fits a 220 mm bed whole (one arm with its hub does). Stylised, assumed material constants.
How should a laundry robot pick one garment out of a tangled dryer load? In a stylised disc-pile model aiming at a visible opening takes 13.4 assumed seconds per garment against 22.7 for pinching the top and regrasping, and pushing garments aside first is slower (17.7 s); one arm then serves 151, 110 and 127 items an hour. Assumed times, not a robot.
How long may a laundry robot spend finding a garment's opening before blind pinching is faster? On paired piles of the stylised pick model, aiming wins only if the detector costs under about 9 s per pick (95% interval 8.9 to 9.6, assumed times); the limit falls as regrasps get likelier to succeed or more openings are hidden. Stylised.
How often may a laundry robot's opening detector aim wrong before blind pinching is faster? In the stylised hanger-pick model each 10 points of detector error cost about 1 s of look-time budget: 9.2 s per pick when perfect, 4.5 s at 50% wrong, none when always wrong. Stylised.
Does the 2D hanger result survive in 3D? With an arm as deep as the garment a 3D cloth sheet matches the 2D drape (within 0.05 cm for round-ended hangers) and the best width is again 1 cm over the half shoulder; a shallow arm lets the front and back panels fall 5–8 cm and raises a wooden hanger's error from 0.4 to 2.0 cm. Stylised.
No: with caps of 10 and 15 cm the whole-sheet error is 1.08 and 1.21 cm against 1.12 cm at 6 cm (8 seeds each, p = 0.77 and 0.57), so the optimum sat on a flat ridge. Stylised.
Yes, by 0.26 cm on the whole sheet with hanger-fit's bounds (8 seeds each, p = 0.03) and by 0.68 cm once the end-radius and bow limits are widened (p < 0.001), but the 3D-designed hangers have a worse centre line. Stylised.
Does a second laundry-hanging arm lose less if it picks a free garment instead of waiting? At 0.30 m clearance blind pinching recovers 9.5 of its 28 lost garments an hour (151 to 161), aiming about 2 of 10; at 0.45 m nothing. Stylised: clearance and spacing assumed.
Is a laundry-hanging arm's gain from picking a free garment real? Paired on 2000 loads at 0.30 m: aiming +1.25 an hour (0.60 to 1.92), sweeping +4.4, pinching +10.0; at 0.45 m aiming gains nothing. Stylised: inputs are placeholders.
How many dryers can one laundry-hanging arm serve once the pick is simulated, not assumed? A one-arm cell drops from 169 to 147 garments an hour (5.1 to 4.4 dryers) with look-then-aim picking and to 104 with blind pinching; with two arms the fold table is the limit. Stylised.
How many dryers can a laundry-hanging arm serve when folding takes as long as published robots take? At SpeedFolding's 90–120 s per fold the learned-rule cell falls from 169 to 58–44 garments an hour; always hanging holds 146. Only the fold time is sourced.
How many dryers can a laundry-hanging cell serve when its fold station runs at published robot speeds? Timed from the SpeedFolding paper (68 to 167 s per garment) rather than an assumed 25 s, one arm and one fold table serve 0.8 to 2.1 dryers instead of 5.1, and with two arms five dryers need 3 to 10 fold tables. Fold times are sourced; every other station time is still assumed.
Does "arm 1 cm wider than the half shoulder" hold on four fabrics with published KES-FB bending rigidity (0.0066–0.125) and weight (12.5–24.6 mg/cm²)? Best offset is +1 cm in all 12 cases (with stretch swept 40–800 N/m); heavy suiting at 40 N/m nearly ties with +2 cm. B and weight sourced; stretch swept; tee geometry assumed.
Does it matter that the garment a robot picks is also the garment it decides to hang or fold? Linking them moves a one-arm cell from 147 to 141 garments an hour, but two arms swing from 141 to 250 with an assumed kind-to-archetype map. Stylised.
Does the hanger that hanger-fit's CMA-ES designs change for stretchy, heavy knits? The best arm width moves from +0.9 cm past the half shoulder (tee) to +1.5–1.8 cm (EA 40 N/m), but slope, bow and end radius are not pinned down at 150 scores; a tee hanger scores 1.06 cm on a soft double-weight knit against 0.52 cm for one designed for it. Fabric constants swept, not measured.
Should a laundry-hanging arm also steer clear of the other arm's next pick? No: paired on 1000 loads, lookahead loses to avoiding the current pick in 14 of 18 settings and ties in 4, by up to 11 an hour. Stylised: inputs are placeholders.
What does it cost two laundry-hanging arms to empty one dryer pile and wait for each other? Blocking at 0.30 m clearance takes aiming from 201 to 191 garments an hour and blind pinching from 179 to 151; a third arm adds only 3 to 5. Stylised: clearance and spacing assumed.
Can a laundry hanger be printed in two halves on a 220 mm bed, and is the bolted joint strong enough? A half-lap hub joint with two M4 bolts lets every width up to XXL print on a 220 mm bed; the joint (safety factor 3.7–13) is then weaker than the arm (40–70), and printed pegs fail. Stylised, assumed material constants; nothing printed.
Does hanger-fit's "arm 1 cm wider than the half shoulder" survive 162 swept fabrics (bending rigidity 0.003–1, weight ×0.5–2, stretch 40–800 N/m, strip depth 10–30 cm)? Best offset is +1 cm in 151 and +2 cm in 11, all of them stretch 40 N/m; bending rigidity alone moves the best error under 10%. Constants swept, not sourced.
Does a second 3D cloth model, wrapped over the arm, agree with the 2D hanger drape? On the cases both run, it picks the same best arm width (22.8 cm for a size M tee; error correlation 0.994) and adds the bend across the arm (119 deg/cm over a 0.5 cm arm, 34 over a 2 cm one), but disagrees for a heavy knit on a thin arm and is not grid-converged. Stylised.
Should an arm yield to the other arm's next pick only when the clash would be long? Gating by predicted overlap removes most of lookahead's loss and gains +0.7 to +1.35 garments an hour for pinching at 0.30 m (paired, 1000 loads). Stylised: inputs are placeholders.
What LLMs make possible with interviews, open-ended survey answers, reviews and tickets, and when counts built from an LLM's codes can be trusted. Topic page →
Can you do machine learning on qualitative data with an LLM, and when can you trust the numbers? Simulated LLM coders with known error: an 89%-accurate coder (κ = 0.72) understates a 30% code at 26% with 0% interval coverage, and when it reads one group's answers less accurately the naive group gap has the wrong sign (+3.6 against −4 points, "significant" 80% of the time). Prediction-powered inference with 200 hand-coded answers per group removes the bias and narrows intervals 23–26% against hand-coding alone, but is wider below ~80% coder accuracy. Stdlib tool (κ, Krippendorff's α, PPI). Simulated, no real model.
What happens to a regression coefficient when the regressor is an LLM's code? Naive OLS gives 0.74 for a true 1.00 (0% coverage) and biases a perfectly measured covariate when coder error depends on it; DSL with ~210 hand-coded items fixes both (coverage 94–97%) but narrows the coded coefficient's interval only 14%; per-class PPI fixes 3-class shares. Simulated coders.
Does the prediction-powered correction work on real hand-coded text? On 3,188 GoEmotions comments a naive-Bayes coder (kappa 0.14) is wrong on prevalence (13% against 25%, 0% coverage) and overstates a length gap six-fold; PPI repairs both but is wider than hand-coding alone. Not an LLM (no key).
Research programme: valid inference from LLM-coded qualitative data under group shift and rare categories; on 44,485 real tweets a pooled PPI interval covers as little as 67% when the audit's language mix differs from the corpus, a language-stratified one 94 to 96%
How well does an LLM-style coder count negative emotion in real comments? The Claude session agent, coding 300 GoEmotions comments blind, flags 44% as negative against a human 23% (opposite error to the classical stand-ins); accuracy 0.71 matches naive Bayes and trails a word list, and prediction-powered inference stays valid but 29% wider than hand-coding. One reader, not an API model.
Does an automated coder's error differ across languages? On 44,485 real tweets in Hausa, Igbo, Nigerian Pidgin and Yoruba, an English word-list coder and an English-trained classifier read almost none of the negative sentiment in Hausa, Igbo and Yoruba (sensitivity 0.4–11%), flipping some language gaps' sign (Hausa–Yoruba +10.6 points true, −6.5 reported); PPI keeps coverage at 93–96% but is never narrower than hand-coding. Not an LLM (no key)
How big must a hand-coded audit be before you can trust a coder's counts? On 3,188 GoEmotions comments, a tight equivalence test never passed the coder and a loose one passed it too often (coverage 0.35 at 1,600 audited items). Not an LLM; one corpus.
Do a dozen codebook codes predict better than bag-of-words when labels are scarce? On GoEmotions, 12 word-list codes reached 0.65 AUC at 100 labels against 0.56 for bag-of-words, and still led at 1,600 (0.75 against 0.67). Word lists, not an LLM; no learned embedding tested.
Do LLM-style qualitative codes predict outcomes better than bag-of-words at the same labelling budget? On 5,313 GoEmotions comments, not for a reply-vs-top-level outcome: emotion codes (human, an upper bound) reach AUC 0.527 against 0.557 for words and 0.595 for LSA, and 5% coder error erases their gain. All sets are weak; not an LLM.
Does a hand-coded audit protect a group gap when it only checks the overall count? On 3,188 GoEmotions comments, a coder with zero overall bias still distorted a short-vs-long gap by 0.20, and the overall-bias gate covered the gap 0.4% of the time at 1,600 audited items. Not an LLM; one corpus.
Can you estimate a group gap from an audit that hand-codes only a few of the coder's negatives? Not usefully: 0.9-wide intervals at 5 items, and a plain random audit (0.23 wide) beats the design. Pooling the groups' negatives covers 3%. 3,188 GoEmotions comments, not an LLM.
If a hand-coded audit finds no bias in a coder, can you trust its counts? On 3,188 GoEmotions comments, an audit-then-trust rule covered the truth in 8% of draws for a coder 2.6 points off, while always applying the prediction-powered correction covered 94–97%. Not an LLM; one corpus.
Does a low audit rate for coder-negatives pay when the coder has high recall? On 3,188 GoEmotions comments the best share falls with recall (50%, 20%, 2%), but the narrowest interval (0.115–0.119 at 200 items) only matches a random audit with no coder (0.1195). Not an LLM.
Do hypotheses about what separates two sets of documents survive a held-out check? On 5,313 GoEmotions comments a word-counting proposer's effects are 7.6× too large at 100 discovery comments (1.5× at 2,000); a BH check on 3,000 held-out comments confirms almost nothing with shuffled labels, but 36–59% of confirmed hypotheses are the label's own vocabulary. Not an LLM proposer.
How much of a human emotion codebook does a codebook induced from the text alone recover? On 5,313 GoEmotions comments, NMF and k-means codebooks agree with the human emotion label above chance but weakly (NMI 0.26 vs 0.12 for 27 codes); the best single code per emotion reaches AUC about 0.6. Topic models, not an LLM.
Should you hand-code only what the coder called positive, or sample the audit by the coder's label? On 3,188 GoEmotions comments, a positives-only audit had 0 of 1,000 intervals covering the truth for every coder (it misses the coder's false negatives); stratifying by label barely helped. Not an LLM; one corpus.
Can you audit the coder's negatives at a lower rate and weight them back? On 3,188 GoEmotions comments, weighting removes the bias of a positives-only audit but the interval widens as the negative share falls (0.126 at 50%, 0.352 at 5%, 200 items) and under-covers below ~10%. Not an LLM; coders miss half the positives.
With six groups, how many hand-coded items does it take for every group's prevalence to be right? On 3,188 GoEmotions comments, six 95% intervals covered all six truths in only 71 to 77% of 120 to 240-item equal audits (Bonferroni: 89 to 94%); a random audit could not estimate a 1.5% group at all. Not an LLM; one corpus.
How many of the coder's negatives must you hand-code to recover the positives it missed? On 3,188 GoEmotions comments, about 50: coverage was 0.29 with 2, 0.87 with 10 and 0.94 with 50, whatever the audit's total size. Not an LLM; one corpus.
Which confidence interval is right when you hand-code only 5 to 20 of the coder's negatives? Not Wald: 0.63 coverage at 5 items against 0.94 for Wilson or Jeffreys on 3,188 GoEmotions comments. Not an LLM; one corpus.
Does equal-numbers stratified auditing still match the optimal split when the coder errs more in the rare group? On 3,188 GoEmotions comments, injecting up to 30% extra label flips in the rarest 11% group moved the optimal audit share only from 0.53 to 0.56, and equal numbers stayed within 0.7% of optimal width. Not an LLM.
Does a coder's error depend on writing register, and can a hand-coded sample tell? On 3,188 GoEmotions comments, error differs by 1.9 points (naive-Bayes) or none (lexicon) between formal and informal text, yet the naive register gap is three times too large; an audit with up to 800 hand-coded items flags it no more often than chance. Not an LLM (no key); register is a proxy, not a dialect.
Should the hand-coded audit for a group gap be stratified by group? On 3,188 GoEmotions comments, it made no difference for a 36% group and a random audit gave intervals 1.7 times as wide for an 11% group at 100 items. Equal numbers per group matched the optimal split. Not an LLM; one corpus.
Which residential construction tasks off-the-shelf and purpose-built robots can do, alone or beside a crew, learned and checked in physics simulation, and what that would take off the cost of a new home. Topic page →
Research programme: LightGBM quantile models beat the per-city, per-type empirical-quantile baseline on pinball loss in 13 of 15 city/target/quantile cells (2024 test year, Chicago, San Francisco, Austin); Chicago's tails are the exception
Can a stock humanoid carry a stud faster than a labourer? A MuJoCo single-support step envelope: the G1 steps 0.50 m with one 2x4 and cannot carry two; the H1 steps 0.20 m with one and 0.10 m with 15 kg; neither beats a labourer who takes a bundle of four, and the model is restrictive (no falls, drops or energy scored).
Does moving the planned centre of pressure along the sole raise a humanoid's carry speed? Not by a constant offset: the G1's 4 kg result moves one grid cell (0.10 to 0.13 m/s) and joint torques, not the sole, set the limit.
Can a stock Unitree G1 or H1 carry a stud as fast as a labourer? A pendulum gait with no trunk compensation gets the G1 to 0.25 m/s unloaded and 0.10 m/s at 4 kg; a robot with one piece per trip would need 4-13 m/s to match a labourer carrying three.
Does a heel-to-toe sweep of the planned centre of pressure raise a humanoid's carry speed? No: one grid cell for the G1 at 4 kg and the unloaded H1, and nothing for heavier loads, because joint torques set the limit.
Can a stock Unitree G1 or H1 hold one end of a sheet while a person lifts the other? For a 22 kg sheet the person carries 11.1-11.5 kg-equivalent in a 2-4 s lift; the G1 manages up to 8 kg, the H1 a 23 kg drywall sheet; lag sets the tilt (2-6 degrees at 0.2-0.5 s).
Does a stock humanoid pay for itself on a house site? The break-even slowdown against a $38/h loaded carpenter is about 2.4 for a $16k Unitree G1 and 1.1 for a $90k H1; over a sweep the G1 saves money in 15% of draws, the H1 in 0.4%, and a perfect H1 would remove 0.19% of an average home's price on the taskbook scope (inputs swept, not measured).
Does a purpose-built nailing gantry beat a stock humanoid at fastening sheathing? A modelled two-axis bridge nails a 62-nail sheet in 61 s (6.1x hand nailing); a $100k machine needs about 150 houses a year to break even on walls (50 with roof cassettes), where the H1 saves money in 0.4% of draws (price and times swept, not sourced).
Can a stock Unitree G1 or H1 push a nailer into a wall and place nails inside a stud face? One 4x8 sheet is 62 nails, 34 with a +-3.9 mm window; the tip needs 1.24 mm scatter for a 95% sheet. The G1 pushes up to 142 N and reaches 18 of 62 nails from one stance, the H1 up to 276 N and 36 of 62 (static, peak torque, no policy).
Can a G1 humanoid nail a 4x8 sheet lying flat on a table? Not better than on a wall: pushing down at 50 N with its feet planted it holds only 30 of 693 reach cells, reaching 48 of the sheet's 62 nails in 16 stances (13 stances for all 62 on a wall), and matching hand nailing (372 s) only if each re-stance takes under 23-24 s (push, standoff and re-stance time are swept, not sourced; static IK, no walking).
With simulated carry and nailing results in place of a swept slowdown, does a stock humanoid pay on a house site? The H1's carry slowdown is 0.41 to 1.70 against a one-stud labourer (pays in 72% of cells) and 1.63 to 6.82 against a bundle carrier (never pays), against a break-even of 1.07; the dollars are tens per house.
Can a stock humanoid hold a stud for a minute? G1 static joint torques re-read against a swept continuous-torque fraction: the waist is at 0.54 of peak with empty hands at the carry pose and 0.91 with a 3.8 kg stud, so below a 0.6 continuous ratio nothing is sustainable (0.6 kg at 0.6) and a stud reaches the winding limit in 0.14 thermal time constants at 1/3. A 150-pose search finds a posture (hands 0.15 m ahead, 0.7 m high) at 0.33 of peak, so the 0.91 is not the floor.
Does a searched arm and waist posture let a G1 hold a stud longer? In MuJoCo the stud's peak joint fraction falls from 0.91 (default) to 0.76 with the centre of pressure on the sole point and to 0.49 (best of three noisy seeds) 3 cm inside the toe edge, enough to make a stud sustainable at a continuous rating of 0.5 of peak; a 2x6 goes 0.93 to 0.68 and sheets stay above peak.
Does the hand-written flexing-sheet plant of buildbot-skills agree with MuJoCo? Pass/fail labels agree on 99.8% of 2600 episodes across 13 policies, so the sim-to-sim transfer failure (0-11% vs 81% where tuned) is not an artefact of my equations.
Does a G1 on a drive-and-lift base nail a 4x8 sheet faster than a walking G1? Yes in 22 of 24 speed settings: 54-121 s a sheet (13 stances, 12 moves of 5-63 s) against 85-119 s walking and 372 s by hand, and it matches a 61 s gantry only with a fast tip, 0.5 m/s drive and 0.2 m/s lift (speeds swept, not a chosen machine; reach unchanged from static statics).
How slow must a person be at nailing a sheet of sheathing for a Unitree G1 nailing it to pay? A walking G1 (85 s a sheet) pays above 35 s of person time at 0.3 supervision, a base-mounted one above 26 to 76 s; about $110 a house, and the person's time per sheet is the unsourced unknown.
Does a nailer's recoil slow a G1 down when it fires a whole 62-nail sheet in sequence? Not by much: the arm is settled and back on the wall within 0.31 s at 4 N s of recoil, shorter than the 0.16 s moves only for a fast tip, so a sheet loses 0 s (2.3-2.5 s at 10 m/s2 and 4 N s) and the clean-sheet probability does not move; the stud finder still sets the budget (recoil, loop, tip speed and wall are swept, not sourced).
Can a stock humanoid carry building materials? MuJoCo static payload envelopes of the Unitree G1 (median 4.5 kg, waist-limited; matches Unitree's 2–3 kg rating) and H1 (median 14.2 kg, elbow-limited): the G1 can carry a 2x4 but not a 2x6, the H1 can take one end of an OSB or drywall sheet with a person and set a lightweight block, but not a whole sheet, a normal-weight block or a 60 lb bag, and neither reaches an 8 ft ceiling.
Does a framing nailer's recoil knock a stock Unitree G1 arm off the stud window? In a closed-loop MuJoCo hold, up to 4 N s of recoil moves the tip 1-4 mm (window +-3.9 mm) but 1 N s or more lifts the nosepiece off the wall for 25-140 ms; stiff loops go unstable with 10-20 ms delay (recoil, delay and wall are swept, not sourced).
How well must a drywall-screwing robot find the framing? A 4x8 sheet (28 wall screws, 36 ceiling) needs one read per member good to 1.0 mm for 95% clean sheets, nearly the nailing figure; allowing 3 missed screws gives 1.7 mm, averaging 4 reads 2.1 mm.
How many hours of an 8-hour shift can a battery-powered Unitree G1 work? One 421 Wh pack gives 4.7 h; two packs and one charger give 7.7 h; above about 300 W the charger is the limit, and pack logistics move the cost break-even only from 2.42 to 2.27 to 2.46 (draw swept, not measured).
Can the building-site robot skills ship as loadable files? Five JSON skill files reload and re-score exactly; a follow skill tuned on the worse of two plants passes 68%, 65% and 70% on the rigid, flexing and MuJoCo plants, no better than tuning on the flexing plant alone (72%, 69%, 71%).
Does a sheet-following skill tuned on a rigid-sheet simulator survive a flexing sheet with delay? It passes 81% of episodes where it was tuned and 0-11% on the held-out plant; tuning on the held-out plant gives 61-66% there.
How many times must a G1 humanoid re-stand to nail one 4x8 sheet? About 13 stances at 5 platform heights: with its feet planted it holds a 3.4 kg nailer at 50 N only 0.7-1.5 m high and 0.3 m sideways, so one stance covers at best 6 of 62 nails, and the sheet matches hand nailing (372 s) only if each re-stance takes under 26-29 s (push to seat and re-stance time are swept, not sourced; no walking simulated).
How well must a nailing robot find the studs? A 4x8 sheet needs a single stud reading good to 0.89 mm (1 sigma) for 95% clean sheets; a stud finder's 'within 1/8 in' claim gives 28% (8 of 62 nails missed) or 69%; averaging reads and pooling a straight wall help, re-measuring each nail is worst.
Which house-building tasks hold the crew hours, and which can a stock humanoid hold the load for? An open task book of a 28x40 ft wood-frame house: 20 tasks with cycles, masses, tolerances and crew-hours, scored against the simulated Unitree G1 and H1 payload envelopes; fastening is 31% of the hours, and the H1 passes the payload test for 53-81% of them (minutes per unit are assumptions, swept).
Which joint's torque limit caps a stock humanoid's carrying? For the G1 it is the waist pitch: doubling it alone takes the heaviest feasible payload from 4 to 6 kg; the H1 has no single bottleneck.
Simulated societies at scale: how opinions, norms and cultures form, split and spread, and which interventions change the path of a large group of people, tested across the modelling assumptions nobody has measured. Topic page →
Which interventions bring a polarized society back together? In an opinion-dynamics model with backfire swept from none to strong, bridging ties across camps never merges them and at a rejection threshold of 0.7 rewiring 10% of ties drives everyone to the extremes, while a ladder of committed voices within reach merges them in 24 of 25 settings (moderate broadcast 19, nudge 14, tolerance 8, bridging 2); interactive simulator included (tolerance and backfire are swept, not measured).
Cited syntheses of the historical, archaeological and social-scientific record on big human questions: what the evidence shows, what replicated, and how different scholarly and theological lenses read it. Topic page →
A heavily cited synthesis of the evidence on how religion developed, from the cognitive science of belief and Palaeolithic burials through Göbekli Tepe, the first states, the Axial Age, Israelite monotheism, the Big Gods debate, early Christianity and the East–West Schism to 2020s data, read through scientific, historical and Catholic and Orthodox theological lenses, with what replicated and what did not
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