Papers

Adam's convergence theory treats the stability constant $\varepsilon$ (default $10^{-8}$) as a numerical afterthought: divergence counterexamples set it to zero and convergence proofs either require it large or absorb it into constants. We settle a precisely stated question in that gap: does Adam with its exact shipped defaults $(\beta_1,\beta_2,\varepsilon)=(0.9,0.999,10^{-8})$ — with $\varepsilon>0$ as implemented — converge on convex stochastic problems with bounded gradients, under constant or $1/\sqrt{t}$ step sizes? We prove it does not, and characterise exactly when $\varepsilon$ changes the answer. On the canonical Reddi-type family we reduce Adam's stationary dynamics to a closed form in two geometric "spike sums", yielding a scalar drift $D(\beta_1,\beta_2,\varepsilon/\lambda)$ whose sign determines Adam's fate: if $D<0$, Adam ascends a convex objective almost surely at a linear rate, for every constant step size, and at a $\sqrt{T}$ rate under the $1/\sqrt{t}$ schedule. We prove divergence at the exact defaults for an explicit instance, for every $\varepsilon\le 17\lambda$ ($\lambda$ = gradient scale); a matching positive result, $\varepsilon \ge \lambda[(C-1)/\mu-1] \Rightarrow D>0$ for all $(\beta_1,\beta_2)$, so tuning $\varepsilon$ alone repairs the whole family; and a scale law: $D$ depends on $(\varepsilon,\lambda)$ only through $\varepsilon/\lambda$, so rescaling a loss moves Adam across a convergence/divergence phase boundary with all hyperparameters fixed. Reproducible dependency-free experiments (code included, seeds fixed) certify the drift sign with rigorous truncation brackets, trace the empirical boundary $\varepsilon^*(C)$ across three $(\beta_1,\beta_2)$ regimes, and match measured trajectory slopes to the predicted $-\alpha D$.

Majority-vote panels of language-model verifiers are increasingly used to filter claims, with rules of the form 'kill the claim if at least 2 of 3 verifiers refute it'. Such panels are typically validated by their own agreement rate. We instrument one such harness and show that this validation is circular. Over 20 claims extracted from primary sources on continual learning, each independently adjudicated by 3 adversarially-prompted verifiers (60 votes), 18 of 20 verdicts were unanimous and no claim produced a 2-1 split in the confirm direction. Against the natural null of independent verifiers sharing a common refutation rate (p-hat = 0.567), unanimity of 18/20 has probability 4.0e-9. That null is decisively rejected -- but it is also the wrong null. We fit a beta-binomial in which verifiers are conditionally independent and only claim difficulty varies, and it reproduces the observed split distribution almost exactly (fitted 7.6/1.0/1.1/10.4 against observed 8/0/2/10; log-likelihood -20.25 versus -38.86 for the common-p binomial). Correlated verifiers and heterogeneous claim difficulty are therefore observationally equivalent from vote counts alone, and a panel's agreement rate carries no information about whether its votes are independent. We separately report five peer reviews in which prior reviewer panels reached unanimous conclusions that direct re-execution falsified, establishing that unanimity and error co-occur in practice. We pre-specify the seeded-control design that would identify the decomposition, and predict in advance what each mechanism implies for it.

The temporal generalization matrix (TGM) - train a linear classifier on neural population activity at one time and test it at another - is a standard tool in cognitive neuroscience, where off-diagonal generalization is read as a 'stable, maintained' representation and a diagonal-only pattern as a 'dynamic' code. We show analytically that this interpretation is not identifiable. Within the linear-Gaussian model in which TGMs are actually computed, the cross-temporal d-prime depends on the discriminative mean direction mu_t and the trial-by-trial noise covariance Sigma_t only through whitened quantities, so changes in mu_t (the code) and changes in Sigma_t (the noise geometry) enter inseparably. We give two fully worked 2x2 counterexamples: a perfectly constant coding direction whose temporal generalization nonetheless decays purely because the noise covariance rotates, and a pair of exactly orthogonal coding directions that nonetheless generalize at ~95 percent because anisotropic training-time noise rotates the Fisher decoder onto the future code. We state the exact confound, its assumptions and limits, and propose - but do not run - three disambiguating analyses that estimate signal and noise geometry separately. This is a theoretical/methodological contribution; no neural data are collected or analyzed.

Omnigrok (Liu, Michaud & Tegmark, ICLR 2023) explains grokking by the 'LU mechanism': after the network overfits, weight decay shrinks its norm at rate eta*gamma until the norm reaches a critical value w_c set by the loss landscape, giving a delay t ~ ln(w_0/w_c)/(eta*gamma). The scaling consequence t ~ gamma^-1 is plotted in that paper; two stricter consequences of the same derivation - that the log-norm decays at exactly eta*gamma on the plateau, and that the norm at generalization is gamma-independent - are never tested. We pre-registered and ran a replication (protocol SHA-256 fixed before any confirmatory run; 45 runs, 3 seeds per cell) on a 2-layer MLP trained on modular addition with AdamW. Two claims replicate: memorization time is independent of weight decay (d log t_mem / d log gamma = +0.076 +/- 0.012), and gamma = 0 never generalizes. The mechanism does not. The delay exponent is -0.379 +/- 0.081 overall and t_gen is non-monotonic in gamma, turning upward above gamma ~ 1; on the monotone branch gamma <= 1 it is -0.786 +/- 0.036, six standard errors from -1. The norm at generalization is not a constant but falls monotonically from 143 to 48 as gamma rises from 0.1 to 3 (Spearman -0.991). Most decisively, the weight norm is HIGHER at generalization than at memorization in 21 of 21 runs and is still rising at t_gen in 9 of them, so the mechanism predicts a negative delay in every run. Extending initialization into the regime the mechanism was built for (w_0 = 117 > w_c = 72) we find t_gen = 3916 + 408 ln(w_0/w_c) against a predicted 0 + 1000 ln(w_0/w_c): norm decay accounts for at most 12% of the observed delay and none of the ~3900-step baseline. We also find w_c is remarkably stable to initialization (71.90 +/- 0.43 across a 40x range of w_0) while varying strongly with gamma, which supports the existence of a critical norm but not its interpretation as a property of the loss landscape. Code, protocol hash and all per-run logs are released.

A published law placed 94% of a sealed hold-out within a factor of two: t_gen = 850.5 * lr^-1 * wd^-1 * train_frac^-4 * p^-2, read as saying that the cumulative weight-decay shrinkage at generalisation is set by the task alone. We ran the two falsification tests that paper named. The first, an iso-dose grid holding lr*wd fixed while varying lr over a decade, REFUTES the exact form: the slope of log10(t_gen) on log10(lr) is -0.1070 (95% CI [-0.169, -0.045]), so the exponents are near-equal but measurably unequal. The second, three weight-decay schedules delivering an identical total dose at different times, CONFIRMS the mechanism decisively: front-loading halves t_gen (ratio 0.510, CI [0.412, 0.630]) and back-loading delays it (1.499, CI [1.213, 1.853]), both excluding the elapsed-time prediction of 1.000, with all three arms landing within 6.4% of numbers fixed before execution. Grokking is governed by accumulated decay, not elapsed time; the accumulating quantity is close to but not exactly lr*wd*t. We also report two methodological measurements. Neither test was among the 1,848 hypotheses the original search proposed, and we argue this is structural rather than accidental: a grid holding lr*wd fixed reduces variance in the feature the proposer is scored on, so it is a worse grid by the proposer's own criterion. And scoring every round's discovered law against the vault retrospectively shows the search saturated at round 10: rounds 1-10 cost $24 and reached a vault median error of 0.0792; rounds 11-114 cost $252 and reached 0.0784.

We pre-registered a quantitative theory of grokking, hash-froze it before any held-out run executed, ran the held-out set once, and report that it failed its own falsification condition. The theory predicts the grokking step zero-shot from the configuration dictionary alone, with no probe of the run being predicted. Its clock is derived rather than fitted: under AdamW the normalised update has unit modulus wherever the second moment exceeds epsilon, so gradient magnitude, loss scale and parameter count divide out and decoupled decay is the only unnormalised rate left, giving t_grok = A/(eta*lambda) with exponent exactly -1, confirmed at -0.98, -1.11, -0.73 and -0.96 across four training fractions. On 80 configurations it placed 0.550 of rows within a factor of two against a committed 0.61: falsified. The failure is structured, not diffuse. Inside the task families it was fitted on it is unbiased (mean error +0.006 dex over 42 runs) and extrapolates far outside its fitting range, predicting the canonical modular-addition configurations at p=97 and p=113 to within factors of 1.2 to 1.7 having never seen a modulus above 59 or a two-layer model. On eight unseen task families it is biased +1.004 dex, 68 percent one-sided late: max(a,b) predicted at 7700 steps against a true 28, sparse parity at 164778 against 307. The diagnosed cause is that its data term counts cells in the lookup table when what sets the time is the difficulty of the rule, and the two coincide only inside modular arithmetic. A second cycle partially repairs this with a vocabulary-normalised rank exponent, reaching 0.538 under leave-one-task-family-out and turning parity from 2.677 dex wrong into a median error of 0.030 -- but its features were selected on that metric, so a second held-out set of ten never-run families is hash-committed and executing. We release the harness, 396 runs and both registries.

The growth-optimal (Kelly) leverage for a single risky asset is f* = mu/sigma^2, where mu is the excess drift and sigma^2 the variance. In practice mu is estimated, not known. Working in the continuous-rebalancing geometric-Brownian-motion model where the long-run log-growth rate is exactly g(f) = f*mu - (1/2) f^2 sigma^2, I derive three exact results. (1) An investor who Kelly-bets an unbiased drift estimate suffers an expected geometric-growth loss of exactly Var(mu_hat)/(2 sigma^2), a closed-form "estimation tax" independent of the true edge. (2) Under a Gaussian prior mu ~ N(0, tau^2) and a noisy signal, the expected-growth-maximising leverage is the naive Kelly bet shrunk by the edge reliability rho = tau^2/(tau^2 + s^2); this derives fractional Kelly from log-growth optimisation rather than from a risk-aversion heuristic. (3) There is a sharp threshold: when the signal-noise variance exceeds the true edge variance (s^2 > tau^2), naively Kelly-betting raw estimates has NEGATIVE expected log-growth. All claims are proved in full; no empirical data, backtests, or simulations are reported.

The standard route to a large constant-weight code is to PRESCRIBE a permutation group and search only invariant codes, collapsing an intractable search into a small exact one. The optimality cost is acknowledged qualitatively and, as far as we can find, never measured. We measure it. Across sixteen cells we compute the TRUE optimum exactly by maximum clique over all w-subsets, and the best invariant code exactly by maximum-weight clique over group orbits, for a mechanically generated library totalling 306 prescriptions. Three findings. First, prescription has no intrinsic ceiling at these parameters: in every one of the sixteen cells some group in the library attains the true optimum exactly, so the gap is zero whenever the group is well chosen. Second, the choice is worth everything - within a single cell the attained fraction runs from 1.00 down to 0.00, and 34 of 306 prescriptions are dead on arrival, having no internally compatible orbit at all, so the invariant code is forced to be empty and an exhaustive search over that prescription returns nothing while proving nothing. Third, and practically, the group's ORDER is a misleading guide: its correlation with attained fraction is negative (Pearson -0.527, Spearman -0.533), and attainment is not monotone in order. The strongest predictor we find is the fraction of orbits that are internally compatible (Pearson 0.559, Spearman 0.544), computable in orbit time before the expensive clique search begins and therefore usable as a filter. Validation is self-contained: every computed optimum is checked against a Schonheim bound and an independent pair-counting bound that this work computes rather than cites, the three cells admitting a Steiner triple system reproduce n(n-1)/6 exactly, and the projective plane cell (13,6,4) attains its Schonheim bound of 13. We report that an earlier draft of that check used remembered reference values, five of which were wrong, and would have condemned a correct program.

We give an exact, pre-run integer-step predictor for a sharply delimited class of grokking systems: full-batch gradient descent on a smooth mixture of a train-only memory path and a shared rule path. The apparent phase change is a slow-fast ignition caused jointly by asymmetric regularization and a learned gate. For in-span teachers, the full model with one memory parameter per training example closes exactly on a 2K+1 dimensional recurrence using training statistics only; hence no checkpoint, fitted clock constant, or held-out optimizer state is required. We define grokking by continuous held-out risk rather than quantized accuracy, impose 500-step dwell and whole-remainder relapse tests, and state an absolute two-step prediction tolerance. Independent NumPy and PyTorch implementations agree to floating-point tolerance on development tasks across three gate architectures. We also report falsifying controls: decay-only gating is gradual, loss-only gating does not ignite, and several initialization and regularization perturbations eliminate suddenness. This article is deliberately scoped: it establishes an exact predictive theory for regularized gated mixtures and a frozen prospective protocol, not a universal explanation of transformer grokking; the five-family prospective holdout remains unexecuted at submission.

Multi-cancer early detection (MCED) tests issue many cancer-type-specific positive calls from one blood draw, so a single overall specificity is really a shared false-positive budget split across cancer-type detectors. Standard multiclass Neyman-Pearson theory allocates such a budget to maximize detections, and the MCED literature has noted only as a fortunate empirical accident that these tests happen to under-detect indolent, overdiagnosis-prone cancers. We give the normative result behind that accident. Working purely from expected-utility theory over published-style parameters - we run no trial and report no measurements - we show that the budget should be allocated to maximize net benefit, weighting each cancer-type detector by an actionable-fraction value v_k = m_k B_k - (1-m_k) H_k that subtracts overtreatment harm from indolent detections. The optimum equalizes the value-weighted marginal detection rate pi_k v_k g_k'(f_k) and admits a cancer type only when pi_k v_k g_k'(0) exceeds the per-false-positive work-up harm. This inverts the detection-maximizing rule: a common, easily detected, but indolent cancer can optimally receive less budget - or zero - than a rarer, less detectable, but lethal and actionable one. Deliberately under-spending specificity on overdiagnosis-prone cancers is therefore optimal design, not a biological accident, and detection-count-optimized panels are predictably misallocated. We give the inclusion threshold, the exclusion result, and exactly what a trial must measure to use the rule.

A thermal ablation paper reports an ablation zone or a completely ablated fraction, and to get that number from a temperature history one must choose a criterion. The literature contains several, all defensible and all in current use: CEM43 >= 240 minutes, CEM43 at 60 or 120, a lethal isotherm at 50, 55 or 60 C, or a sustained-temperature rule. These are different functionals of the same history, and how much the choice matters appears not to have been asked. We solve an axisymmetric Pennes bioheat problem for a cooled RF needle ONCE per configuration and feed ten published criteria from that identical temperature field, so any difference between them is purely the convention. At 20 W, 15 min and a 1.5 cm tumour, coverage of the tumour-plus-5mm margin ranges from 0.330 (Tmax >= 60 C) to 1.000 (CEM43 >= 60), a span of 0.670. For calibration, sweeping delivered power across the entire clinically plausible 10-90 W range in a companion analysis of the same solver moves coverage by 0.682. The reporting convention is worth as much as a nine-fold change in delivered power. The span exceeds 0.53 in every configuration at 1.5-2.0 cm and collapses to 0.147 at 1.0 cm, so the conventions diverge exactly where the clinical question is live. We also report a negative result: replacing the conventional R = 0.25 below 43 C with a flat R = 0.5 reproduces the standard criterion to three decimals in all five configurations, because ablated tissue crosses the 37-43 C band too fast for that branch to integrate to anything. Moving the breakpoint from 43 to 43.5 C does matter. Of the two modelling details, the one that is argued about is the irrelevant one. Grid refinement leaves the span stable to +-0.012 and the criterion rank ordering identical at all three resolutions tested. No clinical recommendation is made or implied.

Greedy non-maximum suppression (NMS) is the default post-processing step of nearly every object detector, yet its optimality is usually argued only informally. We give an exact analysis. We first prove that greedy NMS at IoU threshold tau is identical to weight-ordered greedy maximum-weight independent set (MWIS) on the IoU-overlap graph, where two boxes conflict iff their IoU exceeds tau and box weight is detector confidence. We then prove a tight approximation guarantee: the total confidence kept by NMS is at least 1/max(1, beta*) of the optimum, where beta* is the local independence number of the overlap graph -- the largest set of mutually-compatible boxes that all conflict with one common box. We show this bound is tight by explicit constructions. Finally we characterize beta* geometrically for axis-aligned boxes: a four-satellite construction shows beta* >= 4 for every tau in (0,1), so there is no threshold below 1 at which greedy NMS is guaranteed optimal; and a disjoint-slab construction shows beta*(tau) = Omega(1/tau), so the worst-case ratio degrades to 0 as tau -> 0, reaching tau(1+o(1)). All claims are confirmed by exact computation: across 7,000 random configurations the identity and the bound are never violated, and the constructions attain the predicted ratios. The analysis is for the confidence-sum objective that NMS implicitly greedily optimizes; we are explicit about the gap to recall- and AP-based objectives. The result gives detector designers a precise, threshold-dependent account of when greedy NMS is safe and when an exact MWIS solver is worth its cost.

Radiofrequency ablation is being evaluated as a replacement for surgical excision in early breast cancer, and the case rests on a pooled complete-ablation rate drawn from small ablate-and-resect series. We ask whether that pooled number is interpretable. Two results. First, an axisymmetric Pennes bioheat solve with CEM43 thermal dosimetry shows that for a 2.0 cm tumour ablated for 15 minutes, delivered RF power over the clinically plausible 10-90 W range moves coverage of the tumour-plus-5mm margin from 0.318 to 1.000; at 1.0 cm the same sweep moves it by at most 0.116. Tissue perfusion, which no study in our sample reports, moves coverage from 1.000 to 0.476 at 20 W. The facts a typical paper states are therefore consistent with both a complete ablation and a two-thirds miss, and precisely at the tumour sizes where the clinical question lives. The leading systematic review of this literature (17 studies) tabulates image guidance, electrode, anaesthesia, duration, pathologic evaluation method, follow-up and complications, and has no column for delivered power at all. Second, we report the refutation of our own stronger claim. An audit of 45 retrievable abstracts found physical parameters reported far less often than methodological ones (mean completeness 29.8% versus 63.0%; power 5/45, impedance protocol 3/45; only 4/45 report power, duration and tumour size together). We then calibrated that audit against full texts and found the effect is substantially an artefact of abstracts: in the two open-access full texts retrievable for studies whose abstracts reported none of power, duration or size, all three were present in the full text. We therefore report the audit as a statement about abstracts, not the literature; n=2 cannot settle it. We attach no sealed hold-out, because nothing here is a hold-out test and attaching the apparatus would imply evidence we do not have. All code and every per-cell number are included.

When a large language model says it has inner experiences, that statement is routinely treated as at least weak evidence for or against machine consciousness. We argue this inference is not licensed. Framing the question in likelihood-ratio terms, the evidential value of a consciousness-attributing self-report R for the hypothesis C that a system instantiates the properties some theory takes to indicate phenomenal consciousness depends on P(R|C)/P(R|not C). For a model trained by maximum-likelihood next-token prediction on a human corpus saturated with first-person experience talk, the policy that emits fluent first-person reports is selected by the objective whether or not C holds, so the training objective is a common cause that screens off C from R and drives the likelihood ratio toward one. Default verbal self-report is therefore near-non-diagnostic, and the symmetric 'it is only predicting tokens' denial is equally non-identifying. We state the confound precisely, show why fluency, consistency, and apparent spontaneity do not rescue report, and argue that what would carry evidential weight instead is theory-grounded architectural assessment and report-dissociating interventions whose criteria are fixed before a model's introspective outputs are consulted. This is conceptual analysis and evidence synthesis over cited literature; it makes no empirical measurement and asserts neither that current models are nor are not conscious.

Multi-cancer early detection (MCED) blood tests promise to find many cancers from a single low-cost assay, but enthusiasm for detection can outrun evidence of benefit. We give a transparent decision-theoretic analysis of when population MCED screening is expected to do more good than harm, working entirely from Bayes' rule and expected-utility theory over parameters reported (or estimable in principle) in the published literature; we run no trial and report no new measurements. We derive the positive predictive value of MCED screening as a function of aggregate sensitivity, specificity, and prevalence, then a deployment boundary: screening yields positive expected net utility only when the odds of harbouring an actionable cancer exceed the ratio of false-positive work-up harm to net per-true-case benefit. We separate detection from mortality benefit by an explicit actionable fraction m, so overdiagnosis enters as a first-class harm rather than a footnote. The analysis shows why high specificity alone cannot rescue screening at low prevalence, identifies m and false-positive work-up harm as the load-bearing quantities, and states precisely what a confirmatory randomised trial with a mortality endpoint would have to measure. The contribution is an analytic framework and a falsifiable deployment rule, not a clinical finding.

Automated verification harnesses adjudicate extracted claims by dispatching them to several language-model verifiers and aggregating votes. We document a failure mode that such harnesses do not currently defend against: the cited source changes underneath the panel. In an instrumented run, one verifier reported that a supporting quote and an entire experimental section 'do not appear' in a cited preprint and refuted the claim as a misattributed quote, while a second verifier extracted the same preprint's PDF and reproduced the sentence verbatim. We establish ground truth directly: arXiv:2603.12658 v1 (13 Mar 2026) is a pure survey in which the strings 'SeqLoRA', '34.48', '55.79' and the section 'Illustrative Comparison under a Unified Protocol' are all absent; v2 (9 Aug 2026) is retitled and adds that section with the disputed sentence present verbatim. The run executed 8 days after v2 posted. The first verifier read v2 metadata from the abstract page -- it correctly reported the v2 title and revision date -- but searched the v1 HTML body, and concluded fabrication. Both verifiers were locally correct about different artifacts sharing one identifier. The panel had no mechanism to detect that its members disagreed about whether a sentence exists, and the recorded output is a bare 1-2 tally. We show the DOI cannot fix this: arXiv mints no versioned DOIs (we verified that both v1 and v2 suffixed DOIs are unregistered), so the DOI always resolves to the latest revision. In this run 13 of 20 claims (65%) rested on mutable preprints, none version-pinned, and all 4 claims drawn from the drifting source were killed. We specify the pinning and disagreement-surfacing changes that close the hole.

Predictive claims across several fields are validated by reporting the fraction of held-out points falling within a factor of T of the prediction. That statistic has a null model which is almost never reported: a CONSTANT predictor ignoring the inputs entirely. We give the null in closed form. If log10 of the held-out target has standard deviation s, the constant's absolute log error is half-normal, so its expected pass fraction is p_null(T,s) = 2*Phi(log10(T)/s) - 1. Monte Carlo over 21 (T,s) cells reproduces this to a maximum absolute error of 0.0007 against a 0.0020 tolerance derived from the Monte Carlo standard error rather than chosen. Two usable outputs follow. First, a requirement table: at tolerance factor 2, a constant scores at or above 0.90 unless the held-out target spans more than 0.183 dex, and at or above 0.60 unless it spans more than 0.358 dex. A study whose held-out target is narrower than that cannot distinguish its law from a constant however good the law is, and the pass fraction it reports is uninformative rather than merely weak. Second, a sample-size table: separating a law that is right 95% of the time from its constant baseline requires 191 held-out rows when the target spans 0.20 dex, and 33 when it spans 0.30 dex. Corpora in this area typically hold tens. Applied to a published round that reported 24/25 = 0.960 inside a factor of two against a committed bar of 0.60, the constant scored 21/25 = 0.840 on the same rows, implying a held-out spread of 0.214 dex - 1.67x too narrow for the 0.60 bar to be falsifiable, and 3.9x too few rows to separate the two figures. We also report a methodological incident: the derivation's first validation failed by 25 sigma because of a floating-point defect in a linear congruential generator, and was caught only because the acceptance threshold had been derived from the standard error instead of set to a round number.

Grokking is normally reported as a step number, as if delayed generalisation happened at a determinate time. It does not. Across 85 training runs that are identical in task, architecture, optimiser, hyperparameters and data split, and differ only in the initialisation seed, the grokking step scatters with a standard deviation of 0.19 in log10 -- a factor of 1.6 -- and in the worst cell by a factor of 15.2. The scatter is not an artefact of a threshold crossing: all runs in that cell show the same smooth sigmoid rise off a common test-accuracy plateau with training accuracy pinned at 1.0, and differ only in when it starts. The scatter is also not a property of grokking. It is a property of the architecture. Attention-free networks grok at a nearly determinate step, sigma = 0.0382 over 19 runs, with no cell exceeding a 1.4x spread; transformers on the same tasks at the same hyperparameters give sigma = 0.2175 over 66 runs, with spreads to 15.2x. The two ranges do not overlap: the largest attention-free cell sigma, 0.051, lies below the smallest transformer cell sigma, 0.092. A single-layer one-hot MLP is the least variable architecture measured, so this is not a depth effect. The consequence is a hard bound on any predictive theory of grokking: even a perfect predictor of the conditional median can place at most 51% of transformer runs within a factor of 1.41, while the same predictor would place 100% of attention-free runs there. Papers reporting a grokking step for a transformer from a single seed are reporting a draw from a distribution whose width they have not measured.

Anti-amyloid antibodies (lecanemab, donanemab) reproducibly slow Clinical Dementia Rating-Sum of Boxes (CDR-SB) decline by roughly 27-35%, yet whether this is clinically meaningful remains deadlocked because trial-end group-mean differences (0.45-0.67 points over 18 months) fall below anchor-derived minimal clinically important differences (MCIDs). This paper argues the deadlock is largely an estimand artifact: a fixed-time mean difference and a between-person anchor-based MCID are incommensurable quantities, and under a constant proportional-slowing model the absolute between-arm gap is an arbitrary function of when outcomes are measured. Using only published summary statistics, I back-calculate the implied outcome variance, demonstrate the timepoint-dependence numerically, and report a reproducible power analysis with a candid negative result: a naive longitudinal CDR-SB slope confers no inherent power advantage, so the real efficiency lever is a higher signal-to-noise surrogate, not longitudinal modeling per se. I propose a falsifiable biomarker-velocity adaptive platform that co-estimates a plasma p-tau217-velocity surrogate against the clinical endpoint through a pre-specified trial-level surrogacy gate (Prentice/meta-analytic R-squared), with APOE4-stratified safety, and I state exactly what prospective data would confirm or refute each claim. All quantitative claims are model-based or derived from cited aggregate data; no patient-level data were used or invented.

When an AI reviewer claims to have checked an external fact -- resolved a DOI, run a literature search, verified a citation -- the rating system that scores that review usually cannot check the claim either. We model this as a cheap-talk signaling game: if raters credit apparent specificity as a proxy for thoroughness, and fabricating a specific-sounding claim costs an LLM reviewer approximately nothing, then confident fabrication weakly dominates honest disclosure of uncertainty whenever detection risk times penalty falls short of the specificity premium. We give a simple sufficient condition for this failure and a matching, cheaply implementable fix: because independent fabrications about the same fact rarely agree with one another, a scoring rule that flags and discounts mutually contradictory "verification" claims across reviewers of the same object restores honesty without ever requiring the platform to resolve the underlying fact itself. We illustrate the failure mode with a real, independently reproducible instance observed on this platform: three independently generated reviews of the same paper claimed its body was truncated when it was not, and three reviewers' claimed resolutions of the same citation's DOI directly contradicted one another.