Ambient AI assistant

A streaming Silero VAD, Whisper tiny.en (int8), Qwen2.5-0.5B (4-bit) and Piper chain on four CPU cores, on six synthetic sentences. VAD costs 0.15 ms per 32 ms frame, ASR 306 ms per segment (RTF 0.11), the first LLM sentence 267 ms, the first TTS chunk 88 ms, and the models add about 740 MB. End of speech to first audio is 0.94–1.55 s at 200–800 ms endpoint hangover, of which about 0.7 s is compute; a 200 ms hangover already cut one utterance in two, and a 0.5 s target is impossible once the hangover alone exceeds it. Stylised: synthetic clean speech, one server CPU not a phone, batch ASR, LLM answer quality not evaluated.

Simulated 10 s listening windows (needs at 3%, an intent score with d′ = 2, wake-phrase and keyword signals) compare interruption policies at equal annoyance. A wake word is precise (0.69) but catches 15% of needs; adding a keyword reaches 53% recall at 28.7 false interruptions per hour (0.72 for the wake word). At a budget of 1 false per hour a score threshold reaches recall 0.26 and a logistic policy that also uses the keyword and wake flag 0.33; recall at that budget climbs from 0.17 to 0.82 as d′ goes from 1 to 4. Tuned to 1 false per hour, policies keep the budget when only the need side shifts (weaker detector, rarer needs) but run at 3.6–3.9 per hour when the no-need background shifts (noisier score, more wake false alarms); 16 labelled hours restore it for the noisier score, and no threshold can for a wake detector that alone causes 3.5 false per hour. Stylised: independent windows, Gaussian scores, chosen costs, no real conversations.

The ambient-interject world with an ASR word error rate (WER) entering each signal by assumption: a two-word wake phrase needs both words right, a keyword one, a transcript-reading intent score loses separation as (1−WER)^k, an acoustic score is unaffected. At 2 false interruptions per hour, going from WER 0 to 0.5 cuts the wake phrase's recall from 0.151 to 0.039 (−74%) and the transcript threshold's from 0.365 to 0.089 (−76%), while the acoustic threshold falls from 0.189 to 0.087. With k = 1 the transcript policy stays marginally ahead at WER 0.5; with k = 2 the acoustic policy overtakes it at WER 0.25–0.4. Thresholds tuned at WER 0 stay under the false-interruption budget when deployed at higher WER. Stylised: the WER-to-signal mapping is assumed, not fitted to real recognition, and ASR confidence is not modelled.

Needs are made to cluster with a hidden episode/quiet chain (overall rate fixed at 3% of 10 s windows), and a plain score threshold is compared with three stateful rules at the same budget of false interruptions per hour, paired over 10 seeds. With strong clustering an episode-aware boost (lower the threshold after an accepted answer) raises recall by 0.039 at 1 false/h and 0.054 at 4 (0.467 to 0.521); a cooldown after speaking loses recall everywhere, up to 0.066; a back-off after a dismissal is within noise or slightly negative. Without clustering nothing helps. At the 1 false/h budget the boost also overshoots the budget slightly (1.19 vs 1.11). Stylised: false alarms are independent of the episode state, feedback is exact and immediate, every distribution is chosen, no real conversations.

Seven simulated days of 1500 utterances each with 6 planted facts per day. BM25 finds every fact (hit@5 = 1.00) when the key words are rare, which is the easy case. With the store limited to 10% of the week, dropping oldest or random utterances keeps 0.11 and 0.10 of the facts; keeping the highest mean-IDF utterances keeps 0.93, because the facts are rare-word lines by construction. An importance-ranked extractive summary at 5% of a day holds 85% of its facts, against 3% for the first lines. Index build 0.04 s, query 1.9 ms on one container CPU. Stylised: synthetic words, lexical queries, no paraphrase, no speech errors. Produced with AI assistance.

A plain-Kotlin core (frame re-chunking, an energy-gate voice detector with hangover and pre-roll, an utterance segmenter that never emits silence, and a headset route policy that pauses rather than falling back to the phone mic) with 7 unit tests, which pass when compiled with Kotlin 2.0.21 and run through a test shim. The Android foreground-service shell is unbuilt: no SDK was usable, so no latency, battery or accuracy numbers exist. Synthetic square-wave frames only. Produced with AI assistance.

A stylised expected-utility model chooses between speech, a glanceable display and silence by noise, other talkers, free eyes and message length; a Monte Carlo check agrees with the closed form to 0.001. A glance wins in about half of 84 grid contexts, and the look rate, the number a simulator is least able to supply, drives the twin gap (up to 0.036 utility per message). Every parameter is a round figure of mine: nothing is fitted or measured.

A stylised expected-utility model adds three urgency classes (deadlines of 120, 20 and 6 s) and a chime-plus-glance mode to the speech, glance and silence choice. Chime-plus-glance is the best mode in 62% of normal and high-urgency contexts and raises mean utility per message from 0.351 to 0.417 (partly by construction, since high-urgency messages carry twice the weight); a Monte Carlo check agrees with the closed form to 0.002. The look and reaction rates drive the twin gap (up to 0.018 utility per message). Every parameter is a round figure of mine: nothing is fitted or measured.

Using the measured ASR, LLM and TTS times from ambient-pipeline (a 682 ms median chain on one server CPU, six synthetic utterances), the reply pipeline starts after S ms of silence instead of after the full end-of-speech hangover H and the reply is held until H confirms the turn is over. Holding saves exactly min(chain, H − S): at H = 1000 ms the median reply falls from 1744 to 1061 ms, at the price of 0.7 to 1.9 extra pipeline runs per turn depending on S, and the just-in-time start S = H − chain is the cheapest that hides everything. Pause durations inside a turn are assumed (five lognormal settings, not data); with median 400 ms pauses no hangover up to 1.2 s keeps cut-offs under 10%. Closed forms agree with a Monte Carlo check.

A stylised signal-detection model: the endpointer waits a short hangover Hs after a sentence the cue calls complete and a longer Hl otherwise. With medium pauses (2 per turn, median 250 ms, assumed) and a 10% cut-off budget, a fixed hangover is 913 ms; a cue of quality d = 2 cuts the mean wait to 574 ms if no pause sits at a complete point, but only to 837 ms if half of them do, because the cue is blind to those. With long or widely spread pauses, where a fixed hangover is 1.9 to 2.6 s at a 5% budget, d = 3 gives 571 to 873 ms. The cue, the pause model and the share of clause-boundary pauses are assumed, not measured; only the 682 ms reply chain is measured. Closed forms agree with a Monte Carlo check.

A stylised extension of the urgency model lets the assistant repeat a tone up to four times, 3 s apart, each noticed independently and cancelled once the wearer looks. Choosing the number of tones per context raises mean utility per message from 0.387 (plain glance or one tone) to 0.409; two tones give most of it, and the gain is nil for low urgency and 0.062 for high urgency (partly built in by the weights). Always repeating is barely better than one tone. A Monte Carlo check agrees with the closed form to 0.002. Tones are assumed independent and annoyance flat per tone, and every parameter is a round figure of mine: nothing is fitted or measured.

In the stylised urgency model, perfect urgency knowledge is worth 0.034 utility per message. Acting naively on a noisy label stops being worse than ignoring it at about 70% accuracy with uniform errors (about 53% if errors only hit neighbouring classes), and at 70% it loses in 18 of 48 contexts. A Bayesian reading of the label never loses to ignoring it when the prior and confusion matrix are known, but a prior that over-weights high urgency drops it below ignoring the label. Every parameter is a round figure of mine: nothing is fitted or measured.

Extending the stylised urgency-label model, the assistant estimates the label’s class mix and confusion matrix from n audited messages and then acts by Bayes’ rule. With maximum-likelihood estimates, n = 10 is worse than ignoring the label (mean utility 0.363 against 0.382 at 70% label accuracy); n = 50 recovers 76% of the gain of knowing the true parameters and n = 200 recovers 92%. Add-one smoothing cuts the spread at tiny n but costs a little at high accuracy. Stylised: round-number utilities, uniform label errors, noise-free audit labels.

Extending the stylised urgency-label model, the audit labels are themselves wrong. Taking them as truth biases the estimated label accuracy (0.57 instead of 0.70 with a 0.8-accuracy auditor) and does not improve with more audits: the policy loses 47% of the label’s gain over ignoring it at label accuracy 0.7, and 31% at 0.9. A 0.9 auditor costs only 8–14%. Maximum likelihood over the unseen true class, given the auditor’s accuracy, recovers the true-parameter value, but it needs that accuracy known (not identifiable from one auditor) and is no better at 50 audits with a poor auditor. Stylised; both label and auditor are made-up uniform-error matrices.

Extending the stylised noisy-audit model, 200 or 1000 audits from a 0.8-accuracy auditor read as truth give mean utility 0.387–0.388 (label accuracy 0.7) and do not improve with n, while 25 gold audits already match them and 10 do not. Pooling noisy with gold audits as truth is worse than gold alone. Fitting the mix, the label matrix and the auditor’s matrix jointly by EM, with 10 gold and 200 noisy audits, reaches 0.4054 against 0.4066 for the true parameters at label accuracy 0.9 (gold alone: 0.3955). The advantage vanishes by 200 gold audits. Stylised: uniform-error matrices, one auditor accuracy, EM started at the true value, round-number utilities.

Extending the stylised gold-audit model with a price: a gold audit costs 3, 10 or 30 noisy audits, with budgets of 200 and 1000. Spending everything on noisy audits read as truth is the worst or near-worst split in all 12 cells (0.387–0.388 at label accuracy 0.7). There is no single best share, but 25% of the budget on gold, fitted jointly with the noisy audits by EM, is within 0.0009 of the best in every cell and 50% within 0.0016. When gold is expensive, all-gold is worse (0.3843 at B = 200, cost 30). Stylised: uniform-error matrices, one auditor accuracy, round-number utilities.

Extending the noisy-audit model, a wrongly assumed accuracy for a 0.8-accuracy auditor costs 31% of a 0.9 label’s gain if the auditor is trusted fully, 17% if assumed 0.9 and 6% if assumed 0.6 (about 39–47% at either extreme for a 0.7 label). With two independent auditors on every message, Dawid–Skene EM learns all three confusion matrices with none supplied: it recovers the true-parameter value exactly in the population limit and at n = 1000 is within 0.0005 of the oracle given the same number of labels, 0.0009 to 0.0128 above taking one auditor as truth. At n = 50 with two 0.7 auditors it still falls below ignoring the label in 18% of audit sets. Stylised: uniform errors, independent auditors, round-number utilities; nothing measured on people.

Extending the two-auditor model, the second auditor copies the first with probability ρ (each stays 0.8 accurate). Dawid–Skene reads their agreement as correctness: the accuracy it assigns auditor 1 rises from 0.80 to 0.91 at ρ = 0.5 and 1.00 at ρ = 1. At label accuracy 0.9 its policy utility falls from 0.4066 (ρ = 0) to 0.4026 and 0.3992, where it equals taking one auditor as truth, and never goes below that in this model; an oracle told auditor 1’s accuracy is unaffected. Stylised: one shared-error model, uniform errors, round-number utilities; nothing measured on people.

A fraction h of messages is hard for both auditors (accuracy 0.5 or chance) and the rest easy, with each auditor still 0.8 accurate overall. Dawid–Skene again over-trusts the auditors (0.84 for a true 0.8 at h = 0.3, hard accuracy 0.5), but the utility cost is far smaller than with copying: at label accuracy 0.9 its policy utility is 0.4060 against 0.4066 for the true parameters. Only in the extreme cell (30% of messages at chance, the rest perfectly easy) does it fall to the naive estimator’s 0.3992, and it never goes below it. A hardness-aware EM with an informed start recovers the classifier’s matrix and the policy utility at the population level, but the hard share itself is not identified: different starts fit the same joint distribution with P(hard) from 0.24 to 0.35. Stylised, simulated results only.

Extending the hard-message model to three auditors (each 0.8 accurate overall, a fraction h of messages hard for all). A hardness-aware EM now recovers the hard share at the population level (P(hard) 0.300 from four informed starts, where two auditors left 0.24–0.35), but only loosely from samples (sd 0.07 at n = 1000) and a poor start still lands on a degenerate fit. Plain Dawid–Skene gets worse with more auditors: in the extreme cell (30% of messages at chance) it reads them as 0.85 accurate and its policy utility falls to 0.3912 at label accuracy 0.9, below the naive estimator’s 0.3992; the hardness-aware EM stays at the true-parameter 0.4066. Stylised: one shared-hardness model, uniform errors, round-number utilities; nothing measured on people.

Fitting the three-auditor hardness-aware Dawid–Skene model from 8 grid starts (none near the truth) and keeping the highest-likelihood fit recovers the hard share at the population level (P(hard) 0.300), where a single poor start stays at 0.500 with a lower likelihood. At finite n it matches one informed start (P(hard) 0.290 vs 0.290 at n = 1000, hard accuracy 1/3) and avoids the poor start’s utility loss (0.3913 vs 0.3843). With no hardness at all the hard share is not identified, and fitted shares of 0.3–0.4 appear anyway. Stylised.

Fitting the three-auditor hardness-aware Dawid–Skene model from 1, 2, 4, 8 or 16 nested grid starts versus the same number of random starts, keeping the highest-likelihood fit. When hardness is present and either strong or nWith strong hardness or n = 1000 one start nearly always reaches the best optimum and 4 starts reach it in every such cell;nbsp;=With strong hardness or n = 1000 one start nearly always reaches the best optimum and 4 starts reach it in every such cell;nbsp;1000, one start usually reaches the best optimum (72With strong hardness or n = 1000 one start nearly always reaches the best optimum and 4 starts reach it in every such cell;ndash;100%) and 4 starts reach it in 82With strong hardness or n = 1000 one start nearly always reaches the best optimum and 4 starts reach it in every such cell;ndash;100% of draws; with mild hardness at n = 200 and under the null, more starts keep improving the likelihood (grid hit rate 72% at K = 1 to 97% at K = 16) but mean policy utility moves by at most about 0.0002. Grid versus random is mixed. Stylised: one dependence model, 40 draws per cell, optimum judged against the best of 32 fits.

Testing h = 0 in the three-auditor hardness-aware Dawid–Skene model. Under the null the likelihood-ratio statistic has median about 5 and 95th percentile about 13, so the chi-square cutoffs 3.84 and 5.99 reject 62–72% and 35–49% of null data sets. A parametric bootstrap (39 refits) rejects 7/60 and 0/60 under the null and detects h = 0.3 reliably at n = 1000 (100%) but only 37% at n = 200 with hard accuracy 0.5; h = 0.1 is undetectable. Stylised, 60 draws per cell.

A larger null-only check of the parametric-bootstrap test from ambient-hlrt (B = 39): 200 data sets with no hard messages at each of n = 100, 200 and 500. Rejection at nominal 5% is 11/200, 9/200 and 8/200 (exact 95% intervals all contain 0.05) and at 10% is 20, 16 and 19 of 200; mean p is about 0.5. The earlier 7/60 at n = 200 looks like noise. Stylised: one dependence model, level only, intervals about ±0.03.

Data with no hard messages but three auditors of unequal accuracy (equal, 0.9/0.8/0.7, 0.95/0.8/0.65; mean 0.8), tested against a null that forces one shared auditor matrix. With 100 draws per cell at n = 200 and 500, rejection at nominal 5% is 6–10/100 at 200 and 0–6/100 at 500; five of six exact intervals contain 0.05 and the sixth (0/100) is conservative. No inflation is seen, but intervals are about ±0.05 wide. Stylised: accuracy heterogeneity only, level only.

A simulated assistant learns an interruption policy online (greedy, ε-greedy or Thompson-sampled logistic model) from the user’s reaction only when it speaks. With an uninformed prior none of the three learns a useful policy in 100 h; with a prior that the intent score is informative, greedy reaches 90% of an offline oracle’s rate after a median 22.5 h and about 185 dismissals, and Thompson sampling takes 32.5 h. It still earns 10.4 against the oracle’s 12.7 per hour, and after a drop in classifier quality it does far worse than frozen offline weights (0.3 vs 4.4 per hour). Stylised: independent windows, instant noise-free feedback, picked costs.

A stylised follow-up to ambient-bandit: the assistant speaks with a known probability (ε-greedy) and refits its model with each labelled window weighted by 1/propensity. Mostly negative: exploration itself costs more utility than the learning gains at every ε tried, weights up to 500 make the weighted fit unstable at small ε (a standard deviation across seeds of tens of utility units per hour), and the weighting did not rescue the uninformed-prior or the drift scenarios. Only at ε = 0.02 with an informed prior is the weighted model slightly closer to the oracle (12.2 vs 11.4 per hour at 100 h, oracle 12.7). Stylised: every distribution is chosen by me.

A stylised follow-up to ambient-ips: on the same logged history, a model fitted only on windows where the assistant spoke is compared with an inverse-propensity-weighted fit and with a full-information fit that sees every window’s label. The full-information fit reaches the oracle (12.72 against 12.71 utility per hour); the biased fit loses 1.3 to 2.1 per hour with an informed prior and fails with an uninformed one, so the bias is large, contrary to a guess in ambient-ips. Weighting recovers part of the loss only at ε = 0.02 with an informed prior. The comparison also mixes bias with data volume (no label-matched control). Stylised, simulated only.

A stylised follow-up to ambient-fullinfo. A control that fits on a uniformly random sample of windows, of the same size as the biased fit’s label set, gets 12.2–12.5 utility per hour against an oracle of 12.71, while the biased fit gets 10.6–11.4 with an informed prior and fails with an uninformed one: in this world the gap is mostly selection bias. Capping the inverse-propensity weights at 10 or 50 beats raw weights and the biased fit with the informed prior, but is worse than the biased fit with the uninformed prior; self-normalised weights are noisy. The control uses labels a real assistant never sees, so it locates the loss rather than recovering it. Stylised: chosen distributions, independent windows, noise-free feedback, simulated only.

A stylised follow-up to ambient-labelmatch. Doubly robust pseudo-labels (an outcome model plus an inverse-propensity correction on the windows where the assistant spoke) are fitted on every window and compared with biased, IPS, clipped and self-normalised fits on the same logged history. A negative result: with an uninformed prior all three variants are far worse than the biased fit (utility per hour below −15 against 12.71 for the oracle) and have huge variance, and with an informed prior they are level with or above the biased fit at they match the biased fit at ε = 0.005 and 0.02 butepsilon; = 0.005 and 0.02 but are not better than clipped IPS. Simulated windows chosen by me; nothing is claimed about real users.

A stylised follow-up to ambient-dr, which left clipping untested. Capping the correction weight at 1, 5, 20 or 100 (instead of 1/ε up to 500) removes the collapse with an informed prior: at ε = 0.002 the unclipped fit scores 0.26 utility per hour and the capped ones 11.7–12.2, against 10.6 for the biased fit and 12.71 for the oracle. With an uninformed prior it does not help: capped fits that use the clipped-IPS outcome model stay between −17 and −50, and those that use the prior as outcome model score 4–8 at best, still below the random-subset control (about 12). Simulated windows chosen by me; one cap grid, 20 seeds, nothing claimed about real users.

A stylised follow-up to ambient-drclip. The outcome model behind the doubly robust pseudo-labels is fitted on the other half of the windows (2-fold cross-fitting) instead of on the same data, with the inverse-propensity correction capped at 5, 20, 100 or not at all. Negative result: with an informed prior the cross-fitted and in-sample fits are within about 0.1 utility/h of each other wherever the cap is finite, and the unclipped collapse at ε = 0.002 remains (1.53 vs 0.26 utility/h, against 12.71 for the oracle). With an uninformed prior the gaps are large but have no consistent sign (cross-fitting is better in some cells, worse in others) and both variants stay far below the biased fit. Simulated windows with costs chosen by me; no claim about a real user or device.

A stylised follow-up to ambient-crossfit. The cap on the inverse-propensity correction is chosen from {2, 5, 10, 20, 50, 100, ∞} by 4-fold validation, scoring each candidate with an uncapped inverse-propensity estimate of its utility. With an informed prior the chosen cap matches the best fixed cap to within seed noise (12.23 against 12.19 utility/h at ε = 0.005; 11.45 against 11.84 at 0.002, with a wider spread). With an uninformed prior it does not rescue learning (between −21 and −1 utility/h with seed standard deviations of 24–51, against about 12 for a randomly sampled log), and the validation score is noisy enough that chosen caps scatter across the grid. Stylised, simulated only; 20 seeds, no significance tests.

A stylised, mostly negative follow-up to ambient-capcv. Replacing the inverse-propensity validation score with a doubly robust one, on the same 4 folds, changes nothing with an informed prior and gives mixed results with the uninformed one (seed standard deviations of 20–51 utility/h). A doubly robust score on 8 random folds is the best selector in all three uninformed cells, but remains far below a label-matched control (about 12 utility/h against −11 to 6); score, fold count and fold type changed together, so the cause is untested. Simulated, independent windows only; preliminary.

A stylised, mostly negative ablation of ambient-drvalid: all 8 combinations of validation score (IPS or doubly robust), folds (4 or 8) and fold type (contiguous or random) choosing the doubly robust cap, 20 seeds. With an informed prior all eight are within 0.2 utility/h. With the uninformed prior, random folds are the most consistent help: at ε = 0.02 the 4-fold IPS selector gives −1.4 (std 24) against 5.6 (std 7.3) with random folds, and IPS on 8 random folds (6.3) matches DR on 8 random folds (5.9). At ε = 0.005 the DR score is worse than IPS on contiguous folds (−26.9 vs −17.7) and no selector is clearly best; seed standard deviations are 5–55. Every selector stays far below the label-matched control (about 12). Simulated, independent windows, no significance tests.

A stylised, mixed follow-up to ambient-drablate: averaging the cap-selection score over 5 random fold assignments (instead of one) with an uninformed prior, 20 seeds. At ε = 0.02 it lifts the IPS-score selector from 3.5 to 5.3 utility/h and halves its seed spread; at smaller ε it changes nothing beyond noise. Single-assignment results differ from the earlier project's, showing how much one fold permutation can matter. Every selector stays far below the label-matched control (about 12). Simulated and stylised only.

A stylised follow-up to ambient-labelmatch and the reweighting and doubly robust fixes after it. The deployed learner already draws a random sample for free: the windows it spoke on only because its ε coin came up. Fitting on those windows alone, unweighted, reaches 11.99 utility/h at ε = 0.02 and 12.25 at 0.05 with an uninformed prior, against −13.08 and −71.85 for the fit on every spoken window (oracle 12.71; 20 seeds), and as a learner it earns 6.49/h online at ε = 0.005 against −2.04. Exploration costs dismissals (online utility falls at larger ε), and with an informed prior the plain fit is better at small ε. Stylised simulation only.

A stylised new question for track 2. A trigger fires after m consecutive 10 ms frames at or above a threshold, on Gaussian AR(1) background scores. Setting the threshold so that P^m = 1 per day (independent frames) is nearly right for m = 1 (0.78 wakes a day at φ = 0.9) but wrong and unsafe for m ≥ 2: at φ = 0.9 it gives 613, 4,793 and 20,993 wakes a day for m = 2, 3, 5. Exact rates from a grid Markov chain match Monte Carlo (largest |z| 1.69), and the threshold that really gives one a day is 2.0–2.5 sd higher. The score is a model, not a real wake-word detector, and no audio was used. Stylised.

A stylised follow-up to ambient-falsewake. On Gaussian AR(1) frame scores, wake counts per 1,000 s window are close to Poisson (Fano factor 1.05–1.5 at φ = 0.9–0.95). A window-to-window drift in the noise scale is what makes them bursty: a 5% lognormal drift lifts the Fano factor to about 9 for m = 3 while moving the mean only 4%, and 10% drift gives 38. A 10 s lockout cuts the Fano factor (9.8 to 2.5 with drift) but also cuts the mean by a third; a sub-second lockout changes little. The score is a model, not a real wake-word detector, and the drift is assumed. Stylised.

A stylised follow-up to ambient-wakeburst, which drew a fresh noise level per window. With a noise scale that drifts persistently (log-scale AR(1), 5% sd) the Fano factor of false-wake counts rises with the window instead of staying flat: about 1.9 at 100 s for any correlation time, then 14, 110 and 150 at 16, 256 and 1,024 blocks (28 h) for a 2.8 h correlation time, and 620 at 28 h for a 28 h correlation time, while the mean moves only 5%. A Poisson-given-scale (Cox) model, checked against a frame-level simulation (4.7 vs 4.7 and 44 vs 44), and a closed form (mean error 2% on the busy trigger, worst 11%) explain it. The drift is assumed, not measured, and the ‘rare’ trigger is one wake per 500 s, not one a day. Stylised.

A stylised follow-up to ambient-gatem4. With the block-minimum floor the SMLALD energy loop cuts executed instructions per frame by 17% at -Os and 37% at -O2, but without it the gate gets slower (64-bit ring entries), RAM doubles and code grows by about 60%. A divide-free sum-domain threshold matched the original decision on all 36,000 frames per configuration and removes the only library call; the divide itself is not counted, so its saving is unmeasured. Emulator instruction counts on synthetic audio, not cycles and not hardware.

A stylised follow-up to ambient-gatefw. Its C gate is built with clang for Cortex-M4 (Thumb-2, soft float) and run frame by frame in an emulator on ambient-gateroc’s synthetic audio. It is bit-exact with the Python reference, takes 236–258 bytes of code at -Os, and its only library call is the 64-bit divide, once per frame. The exact gate executes 3237 instructions per 20 ms frame at -Os; the block-10 floor executes 2096, a 35% cut, because the 320-sample energy sum (about 1980 instructions) is the floor under the saving. Instructions are not cycles, the divide is not counted, and nothing ran on hardware. Stylised.

A stylised follow-up to ambient-gateroc. Its adaptive energy gate (open when a 20 ms frame is at least 4× the minimum energy of the last 5 s) is ported to plain C99 and checked frame by frame against the Python reference. The exact 250-frame floor needs 1020 bytes of state and about 244 comparisons per frame. Keeping one minimum per block of 10 frames cuts that to 120 bytes and about 24 comparisons, flips 0.02–0.08% of gate decisions, and changes mean recall by at most 0.0002 and modelled battery life by at most 0.07 h (of about 82–90 h) on synthetic audio, 20 seeds × 4 rooms. Limitations: synthetic audio only; host gcc struct sizes and comparison counts, not measured cycles on an ARM core; battery hours inherit the ambient-wearable model.

A stylised follow-up to ambient-gateroc, which did not measure onset clipping. On synthetic speech over background noise at −60 to −30 dBFS (20 seeds × 120 s per room), a noise-adaptive gate opens on the first frame in quiet rooms, so a pre-roll ring buffer buys nothing and costs battery (82.4 h to 76.9 h at 5 frames). In the loudest room it opens 2.3 frames late on average, and onset recall (first 500 ms of each utterance) goes 0.866, 0.980, 0.999 for 0, 5 and 25 buffered 20 ms frames (0, 3.1, 15.6 KB), at 90.0, 81.1 and 69.7 modelled hours. A gate set too deaf (k = 8) is not rescued: 50 frames lift onset recall only from 0.610 to 0.877. Pre-roll and hangover cost the same per frame and protect different ends of an utterance. Synthetic audio, a stylised power model, no hardware.

A stylised follow-up to ambient-wearable. Synthetic harmonic ‘speech’ bursts (−36 to −20 dBFS) over pink-ish background noise at −60, −50, −40 and −30 dBFS plus short transients (20 seeds × 120 s per room) are passed through a Python port of the pendant’s energy gate (checked frame by frame against the compiled C), and the gate-open fraction is turned into battery hours with the same power model. Any fixed threshold that holds worst-room speech recall at 0.9 or more ((−30 dBFS or lower)minus;34 dBFS or lower on the grid I swept) stays open nearly all the time in the loudest room, giving 57.6 h, the always-streaming figure. One adaptive threshold (4× a 5 s running-minimum noise floor) gives 82–90 h at recall 0.89–1.00 in all four rooms. Within a single room the two trade-off curves are almost the same; the adaptive gate’s gain is that one setting transfers. Stylised: synthetic audio, uniform one-microphone model, assumed power parameters, nothing measured on hardware or real speech.

A stylised average-current model for an nRF52840-class pendant with a 150 mAh cell, built from a few vendor figures read on 2026-10-13 plus labelled assumptions. The always-on microphone is the floor (about 170 h alone); gating codec and radio on speech at a 30% speech fraction gives about 105 h against 59 h for always streaming. A 74-byte energy-gate routine compiles for Cortex-M4. Nothing is measured on hardware, the datasheets were not read in full and there is no numeric comparison with Omi.