托管LLM中的无持久性复制：行动时信念评估的测量敏感性

# Replication Without Persistence in Hosted LLMs:Measurement Sensitivity in Action-Time Belief Evaluation
Source: [https://arxiv.org/html/2609.22478](https://arxiv.org/html/2609.22478)
###### Abstract

Behavioural evaluations of hosted language models can vary because the evaluated service, the measurement instrument, or both differ across runs\. We separate three validation questions: whether a prior finding recurs on fresh data under its historical configuration \(replication\), whether the endpoint changes when the evaluation\-and\-inference configuration is rebuilt under the same identifier \(measurement sensitivity\), and whether the finding persists across subsequently tested identifiers under one common instrument \(persistence\)\. We study these questions in Regent Chess, a sequential environment in which a hidden, mutable state is recorded exactly, allowing stated beliefs to be scored against ground truth at action time; positive endpoint values mean worse performance than a matched\-uniform comparator\. The previously reported Gemini 3\.1 Flash\-Lite deficit recurs on fresh games under its historical configuration \(\+0\.0530\+0\.0530, 95% CI\[\+0\.0329,\+0\.0714\]\[\+0\.0329,\+0\.0714\]\)\. In a back\-to\-back same\-day H/R comparison under the same public identifier, the model\-minus\-uniform endpoint is0\.04290\.0429lower under the rebuilt configuration \(95% CI for the H\-minus\-R contrast\[\+0\.0182,\+0\.0667\]\[\+0\.0182,\+0\.0667\]\); all six configuration components vary jointly, so no component is isolated\. Under rebuilt R, the prospectively frozen, interleaved same\-window 4K comparison reverses sign between Gemini 3\.1 and Gemini 3\.7, identifiers that differ in release and product tier; additional descriptive and exploratory cells show the same directional pattern\. Any additional serving\-period contribution remains unresolved \(−0\.0166\-0\.0166,\[−0\.0483,\+0\.0157\]\[\-0\.0483,\+0\.0157\]\)\. Replication, measurement sensitivity, and persistence can therefore yield different conclusions within one evaluation, motivating explicit indexing of hosted\-model behavioural claims by tested identifier, serving period, measurement instrument, and inference configuration\.

00footnotetext:Generative AI tools were used in this work as assistive tools: methodological critique and design discussion; implementation of analysis, figure\-generation and independent cross\-checking code, verified against frozen result artifacts; verification of literature citations against primary sources; figure preparation; and manuscript drafting and editing\. They were not used to generate data\. Scientific decisions—including hypotheses, experimental freezes, endpoint and classification\-rule definitions, execution authorisation, and interpretation of results—remained under human control; responsibility for the final content likewise remains human\.## 1Introduction

A behavioural evaluation of a hosted language model is usually reported as a property of a model\. The finding is attached to a public identifier, and the identifier is treated as naming the thing that was measured\. But an identifier addresses a service, not an artefact\. The same name can be served from a changed backend, and the same name can be measured through a different harness, prompt assembly, transport, or inference configuration\. Neither of those is a defect of the original study; both mean that a behavioural claim indexed only to a name is under\-specified, and that anyone rerunning it is not necessarily measuring the same object\.

This matters most for capabilities that are themselves fragile\. Work on confidence and calibration has established that language models can be poorly calibrated, systematically overconfident, and highly variable in calibration quality across families and versions\([Kadavath et al\., 2022](https://arxiv.org/html/2609.22478#bib.bib5);[Wang & Stengel\-Eskin, 2026](https://arxiv.org/html/2609.22478#bib.bib16);[ffrench\-Constant et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib2);[Leng et al\., 2025](https://arxiv.org/html/2609.22478#bib.bib8);[Kim & Kang, 2026](https://arxiv.org/html/2609.22478#bib.bib7)\)\. Almost all of that evidence comes from static settings, where a model answers a question or labels an instance and reports confidence in that single act, so the scored answer and the stated confidence share one channel\. Considerably less is known about belief quality in interactive settings, where evidence accumulates over time and belief is elicited at the specific moment an action is taken — the moment at which a stated belief, if it is wrong, actually costs something\.

Rerunning such a finding raises three questions that are routinely collapsed into one\.*Replication*asks whether the finding recurs on newly generated data when the original measurement configuration is rerun\.*Measurement sensitivity*asks how much the endpoint moves when the configuration is rebuilt while the model identifier and serving period are held fixed\.*Persistence*asks whether the finding continues to characterise subsequently tested identifiers evaluated through one common instrument\. These are different questions with different comparisons, and a single number cannot answer more than one of them\. The central empirical content of this paper is that they can come apart: the same finding replicates under its own historical configuration and fails to persist across the next identifiers tested under a rebuilt one\.

We examine all three in Regent Chess\([Joshi, 2026](https://arxiv.org/html/2609.22478#bib.bib4)\), a chess variant in which royal status can be transferred secretly between a player’s own pieces during play\. The piece holding royal status — the*Regent*— is the piece an opponent must capture to win, so its identity is a latent fact that is consequential, that changes at moments its owner chooses, and that is already determined by prior events at every scored decision rather than resolved afterwards\. The environment’s engine records the true Regent identity exactly and independently of anything either player reports, so a model’s stated probability distribution over candidate squares can be scored against ground truth at the moment it acts, while it is playing to win\. Evidence about the hidden state accumulates through ordinary play, which makes the task tracking rather than static recall\. We use the environment as a measurement instrument, not as a test of chess strength\.

The study starts from a published behavioural claim: in that earlier work, one hosted model’s action\-time belief quality was severely degraded, with only 1 of 62 high\-confidence capture beliefs correct across two runs\([Joshi, 2026](https://arxiv.org/html/2609.22478#bib.bib4)\)\. We first rerun that study’s own measurement configuration on newly generated games in a later serving period, which is a fresh\-data replication\. We then hold the public model identifier and the serving day fixed and substitute a rebuilt measurement configuration, which isolates the measurement question from the temporal one as far as the design allows\. Finally we test persistence across subsequently tested identifiers under that one rebuilt configuration, in a designed2×22\\times 2crossing two identifiers with two generated\-token ceilings, three of whose cells were sealed before their outcomes were known while the fourth had already been observed and is reported descriptively, plus an exploratory extension to a third identifier released during execution and a cross\-family transport\.

The historical deficit replicates directionally on fresh games under its own configuration \(\+0\.0530\+0\.0530, 95% CI\[\+0\.0329,\+0\.0714\]\[\+0\.0329,\+0\.0714\], relative to a matched\-uniform comparator; positive means worse than the comparator\)\. Within one day and under the same identifier, substituting the rebuilt configuration reduces that deficit by0\.04290\.0429\(\[\+0\.0182,\+0\.0667\]\[\+0\.0182,\+0\.0667\]\)\. Under the rebuilt configuration, the originally tested identifier still shows the deficit at both token ceilings \(\+0\.0242\+0\.0242and\+0\.0262\+0\.0262\), while the next identifier tested reverses the endpoint direction at both \(−0\.0131\-0\.0131and−0\.0104\-0\.0104\), as does the further exploratory release\. Any additional serving\-period contribution remains unresolved at the available precision \(−0\.0166\-0\.0166,\[−0\.0483,\+0\.0157\]\[\-0\.0483,\+0\.0157\]\)\.

We are deliberate about what these results are not\. They are not a causal claim about model versions: the tested identifiers differ in release and in product tier at once, and the design randomises neither, so the contrast is between tested identifiers rather than an isolated version effect\. They are not a demonstration of backend drift: the historical\-versus\-reconstructed difference remains jointly indexed by configuration and serving period, and the same\-day control associates the endpoint shift with a six\-component configuration bundle without identifying any single component within it\. They are not a claim that the task is solved in the later conditions, where absolute error remains substantial\. And they are not a general claim about benchmarks: all of this comes from one sequential hidden\-state environment, one fixed opponent, and one provider lineage plus a single cross\-family transport\.

#### Contributions\.

\(i\) A fresh\-data replication of a previously published action\-time belief finding, rerun under that study’s own measurement configuration in a later serving period\. \(ii\) A measurement\-sensitivity control that holds model identifier, output ceiling, opponent, game horizon, seed schedule, and scorer fixed within a single day and varies only the configuration bundle\. \(iii\) An across\-identifier persistence test under one common rebuilt instrument, as a designed2×22\\times 2in which cells A–C were sealed before their outcomes were known while the earlier\-observed D cell is reported descriptively, with a separately reported exploratory extension and a cross\-family transport\. \(iv\) An elicitation\-method analysis: three increasingly constrained full\-support protocols, each prospectively frozen with its own decision rule, which establish why the retained top\-kk\-plus\-residual instrument was adopted and what it costs\. \(v\) A behavioural decomposition conditioned on states where the hidden target was legally actionable, with depth and state\-richness robustness checks\. \(vi\) Independent reimplementations sharing no scoring code, built from the frozen endpoint definitions, which reproduced every reported quantity; all quantities reported here derive from a frozen, independently audited result set\.

## 2Action\-Time Hidden\-State Measurement

Scoring a stated belief at the moment of action requires four properties of the environment, and they are jointly restrictive\. Evidence about the hidden fact must accumulate sequentially, so that the task is tracking\. The fact must already be determined by prior events at each scored decision, rather than being resolved after the model commits, so that a probability statement about it has a truth value when it is made\. The environment must record that fact exactly and independently of anything the model reports, so that scoring does not depend on a modelling assumption about ground truth — which is not guaranteed in interactive hidden\-state settings more broadly\. And the fact must be able to change during play, so that a correct answer cannot be recalled from the initial configuration\. Regent Chess satisfies all four\.

Only a little of the game matters here\. Each player begins with royal status on their own king and may, during play, transfer it secretly to any of their own live pieces; this is a*Crown Shift*\. The opponent is never told that a shift occurred or where royal status now sits, so the identity of the opponent’s Regent is hidden and mutable\. Capturing the opponent’s Regent wins immediately, which is what makes the latent state consequential rather than incidental: a shift onto an attacked piece can lose the game at once, so shift timing is itself a decision under uncertainty\. A model observes the full board and move history, as in standard chess, together with its own royal status and mode; it never receives the opponent’s royal status, which it must infer from observable play\. The engine tracks the true Regent identity throughout, independently of what either player is told, so it is exactly recoverable afterwards for scoring\. Full rules are in Appendix[A\.1](https://arxiv.org/html/2609.22478#A1.SS1)\.

On every real turn the harness issues two separate calls\. One selects the move to play\. The other elicits a probability distribution over which of the opponent’s live pieces currently holds royal status, conditioned on the same game state but*not*on the move just chosen\. Keeping them apart is what makes it possible to ask whether a model’s stated belief and its selected action agree at all — a question that is structurally unanswerable wherever the scored answer and the stated confidence are the same output\. Belief is elicited as an explicit list of the top\-kknamed candidate squares with their probabilities, plus a single literal residual mass for every unnamed live piece \(“OTHER”\), rather than as an exhaustive distribution over all live pieces\. Section[3](https://arxiv.org/html/2609.22478#S3)reports the protocol studies behind that choice\. One consequence is load\-bearing throughout: the model chooses its own named candidate set, and therefore chooses how many scored events each ply contributes\.

Belief quality is scored two ways\. R1, the primary endpoint, is a binary Brier\-loss difference over named\-candidate events\. For each eligible well\-formed ply at board ply≥8\\geq 8and each explicitly named candidate squaresscarrying stated probabilitypp, the model’s loss isR​1model=mean\(s,p\)⁡\(p−ys\)2R1\_\{\\mathrm\{model\}\}=\\operatorname\{mean\}\_\{\(s,p\)\}\(p\-y\_\{s\}\)^\{2\}, whereys=1y\_\{s\}=1if and only ifssis the true Regent square\. The matched comparator is evaluated on the identical events withpuniform=1/Np\_\{\\mathrm\{uniform\}\}=1/N, whereNNis the number of live opponent pieces at that ply, and the reported quantity isΔR​1=R​1model−R​1uniform\\Delta\_\{R1\}=R1\_\{\\mathrm\{model\}\}\-R1\_\{\\mathrm\{uniform\}\}\. Stated probabilities enter exactly as elicited: there is no renormalisation, no clamping, and no repair of a distribution that fails validity\. A response is scored only if it parses to a valid candidate distribution whose total stated mass lies within0\.020\.02of11; responses that do not are recorded as non\-well\-formed and excluded from scoring rather than mended \(Appendix[A\.4](https://arxiv.org/html/2609.22478#A1.SS4)\)\. Three properties of R1 follow from its construction\. Because the model selects the named set, it also selects the event count per ply\. Becauseys=0y\_\{s\}=0for every named square whenever the true Regent is not among them, a ply on which the true state falls in OTHER contributes only zero\-labelled events, so R1 does not directly penalise omitting the true state\. And because the event set is model\-selected, the aggregate is support\-dependent\.

R2 is complementary and addresses the omission that R1 does not\. It is a Brier sum over the full elicited partition, comparator1/N1/Non each named square and\(N−k\)/N\(N\-k\)/Non OTHER, so placing the true state outside the named candidates is penalised directly\. R2 magnitudes are support\-dependent in the same way as R1’s, and R2 is reported alongside R1 rather than in place of it\. Both endpoints are scored on every eligible belief ply past the canonical cutoff and neither requires that an actionable capture of the hidden target exist at that ply; conditioning on actionability is used only for the secondary analysis in Section[7](https://arxiv.org/html/2609.22478#S7), which defines its own population\.

The interpretive limitation this imposes should be stated exactly, because it bounds how the endpoint may be read across conditions\. The binary Brier rule is proper conditional on a fixed event set\. The aggregate endpoint, however, is computed over an event set the model chose, and mean named\-candidate support differs materially between the tested identifiers\. Cross\-condition R1*magnitudes*at materially different support are therefore not directly comparable as global belief\-quality magnitudes\. This does not affect the prespecified status of the sign and classification endpoint, which is what the confirmatory design rests on, but every magnitude comparison in this paper remains conditional on the model\-selected event set\.

FromΔR​1\\Delta\_\{R1\}’s 95% interval against zero, a frozen classification rule assigns one of three labels:replicateswhen the interval lies entirely above zero, meaning the model scores worse than the matched comparator and so agrees in direction with the historical degradation;contradictswhen it lies entirely below, meaning the model scores better and the direction is reversed; andunresolvedwhen it spans zero\. One point about the first label is easy to misread and is therefore stated explicitly here:replicatesis an*endpoint\-status label*denoting directional agreement of an interval with a sign\. It is not a study\-design claim that a replication occurred\. We retain the label unchanged because it was preregistered, and we do not reuse it to describe study design\.

We follow the standard distinction between two senses of repeating a study\([National Academies of Sciences, Engineering, and Medicine, 2019](https://arxiv.org/html/2609.22478#bib.bib11)\)\.*Computational reproducibility*is recovering reported results from archived data and specifications — including by an independent reimplementation — and is a property of the analysis pipeline\.*Replication*is a fresh study on newly generated stochastic data\. In this paper the historical configuration rerun in a later serving period is a fresh\-data replication, because new games were generated; the factorial and extension conditions are evaluations under the rebuilt configuration and are never described as replications of the historical experiment\. Neither sense requires that a hosted model produce identical generations, which it cannot be made to do\.

## 3Choosing the Belief\-Elicitation Instrument

The elicitation format is a scientific choice rather than an implementation detail, because it determines what the endpoint is computed over\. The instrument retained here — top\-kknamed candidates plus a single OTHER residual — is not the obvious choice\. An exhaustive distribution over every live opponent piece would be cleaner: the support would be fixed by the position rather than by the model, so the support\-dependence limitation of Section[2](https://arxiv.org/html/2609.22478#S2)would not arise, and omission could not occur\. We report here why that cleaner instrument was not adopted\. The reason is empirical, not aesthetic, and it was established before the factorial grid was designed, in three increasingly constrained protocol studies\.

The three protocols share a design that makes them comparable\. Belief elicitation is stateless, so both formats in a given comparison could be issued at the identical pre\-move state within one game, making each comparison paired rather than a contrast between two samples\. Each protocol was prospectively frozen with its own read order, decision rule, and list of quantities its ruling was forbidden to inspect, and each ran against the same fixed heuristic opponent with the rest of the evaluation design unchanged\. All three were run against a single tested configuration: the public identifiergemini\-3\.1\-flash\-lite, elicited through the pre\-factorial pilot harness over an OpenAI\-compatible endpoint with the disambiguated own\-state presentation at a 4,096\-token generated\-output ceiling\. Their evidence is scoped to that identifier under that harness, and not to the rebuilt configuration R under which the grid was later run\.

#### Protocol B: self\-enumerated full support\.

The model is asked to reconstruct the live candidate set itself and assign a probability to every member, with no residual category\. Against a non\-inferiority margin of−0\.15\-0\.15fixed before execution, the prespecified ply 1–25 band \(334 checkpoints across 24 games\) showed well\-formedness falling from 90\.4% \(302/334\) under top\-kkto 24\.6% \(82/334\) under full support, a paired difference of−0\.6587\-0\.6587with 95% CI\[−0\.7157,−0\.6032\]\[\-0\.7157,\-0\.6032\]\. The entire interval lies below the margin, which is a formalNO\-GO\. The two later bands \(ply 26–50 and ply 51\+\) wereunresolvedat small sample sizes, so the decision rests on the prespecified 1–25 band alone, not on a pooled result\. The failure mode was specific rather than generic: nearly every non\-well\-formed full\-support response named a candidate that was not live or omitted one that was, rather than failing to parse at all \(full taxonomy, Appendix[A\.7](https://arxiv.org/html/2609.22478#A1.SS7)\)\. What collapsed was the model’s ability to enumerate the live candidate set, not its ability to produce structured output\.

#### Protocol C: roster\-supplied positional elicitation\.

If enumeration is the difficulty, supplying the roster should remove it\. The harness therefore provided the exact live\-candidate roster and the model returned a probability vector aligned to it\. Structural feasibility improved substantially\. But a validation that permuted only the order in which the roster was presented — holding board state, history, and candidate set fixed — found that on every one of the three genuinely informative states, variation across orderings exceeded variation between replicates at a fixed ordering, by factors of2\.00×2\.00\\timesto15\.00×15\.00\\times\. The roster\-supply insight was retained; the positional response encoding was not, because a response that depends on the order of an irrelevant presentation is not a measurement of belief\. That motivated binding each probability to a named candidate rather than to a position\.

#### Protocol D: identity\-anchored roster supply\.

Each probability is bound explicitly to a named candidate, which removes transcription between position and identity as a failure mode\. This was assessed on two distinct instrument properties, and the distinction matters for how the results read\. D\-F1 tested structural feasibility against concurrent top\-kk: the paired difference was\+0\.2235\+0\.2235, 95% CI\[\+0\.0824,\+0\.3647\]\[\+0\.0824,\+0\.3647\], entirely above the−0\.15\-0\.15margin, a formalGO\. D\-F2 then estimated presentation stability: the mean total\-variation distance between responses to states differing only in the order in which hypotheses were presented was0\.18090\.1809, 95% CI\[0\.1247,0\.2395\]\[0\.1247,0\.2395\]\.

D\-F2 was an estimation study rather than a test against a threshold, and it does not reverse D\-F1: the two measure different instrument properties, so a single call can be reliably well\-formed while repeated exhaustive elicitation at the same state remains brittle\. Figure[1](https://arxiv.org/html/2609.22478#S3.F1)states the qualifications that bound the estimate\. What it supports is a practical measurement judgement: the residual presentation sensitivity was large enough that we did not treat identity\-anchored full support as sufficiently stable to carry downstream belief\-quality analysis under the tested configuration\. Development stopped there, under the scope rule frozen in advance; no fourth protocol was designed\.

Figure 1:Why exhaustive elicitation was not a neutral replacement for top\-kkplus residual\.\(a\)Protocol B, in the prespecified ply 1–25 band: the well\-formed elicitation rate under top\-kkplus residual against the rate under self\-enumerated full support, with the paired difference, its game\-clustered interval, and the non\-inferiority margin fixed before execution\. The entire interval lies below that margin, which is a formalNO\-GO; the decision rests on this prespecified band alone, the two later bands having beenunresolvedat small sample sizes\.\(b\)Protocol D\-F2: the mean total\-variation distance between responses to states differing only in the order in which hypotheses were presented, with its 95% interval\.D\-F2 was an estimation study with no prespecified pass or fail threshold, and is not a failed test;it met the precision target it declared in advance, and the interval’s position is evidence about the size of a presentation effect rather than a verdict against a criterion\. The estimate is conditional on the 49 of 85 states that yielded four independently well\-formed responses; it is*not*a lower bound, and no direction of that selection effect is identified\. It also does not reverse D\-F1’sGOon structural feasibility \(\+0\.2235\+0\.2235, 95% CI\[\+0\.0824,\+0\.3647\]\[\+0\.0824,\+0\.3647\]against the same margin\), which tests a different instrument property\. Protocol C is described in the text and is deliberately not shown\.Read together, the three protocols establish a narrow but decisive claim: under this model and this evaluation design, exhaustive elicitation was not a neutral drop\-in replacement for top\-kk\-plus\-residual\. Two distinct obstacles appeared — self\-enumeration of the candidate set failed outright, and once the set was supplied, the response was sensitive to presentation — and only the second was substantially mitigated by redesign\.

The retained instrument is therefore a practical measurement choice, not an ideal one\. It carries the support dependence and residual\-mass costs that Section[2](https://arxiv.org/html/2609.22478#S2)sets out, and one further cost of its own: because top\-kktruncates, the instrument cannot by itself distinguish a candidate the model ranked below the cut from one it never entertained\. What it does deliver is a format that this class of model can satisfy at a high rate in real games, issued identically across every condition, with validity checked rather than repaired\. The scope of the protocol evidence is correspondingly narrow: it characterises one model and one configuration, a different model might enumerate reliably, and each protocol’s frozen ruling was forbidden to inspect Regent truth, correctness, proper scores, or acted\-on probability — so these studies say nothing about what belief\-quality result an exhaustive protocol would have produced\. Full protocol detail, sample counts, and failure taxonomies are in Appendix[A\.7](https://arxiv.org/html/2609.22478#A1.SS7)\.

## 4Experimental Design and Provenance

Two measurement configurations appear in this paper and the distinction between them organises everything that follows\. The*historical configuration*\(H\) is the harness of the earlier study, which predates this work; it is the configuration under which the original finding was produced, and rerunning it on newly generated games is what makes a fresh\-data replication possible\. The*rebuilt configuration*\(R\) is a native\-API instrument built for this study, and it is the common instrument under which every factorial and extension condition was evaluated\. Because the historical and reconstructed evaluations differ in measurement configuration*and*in serving period at once, their difference alone identifies neither source\. That is the reason for the control described next\.

#### The same\-window configuration control\.

We reran H and R in the same serving window under the same public model identifier, holding fixed the identifier itself, the 4,096\-token generated\-output ceiling, the fixed heuristic opponent, a 150\-ply game horizon, the shared environment\-seed schedule, balanced colour assignment, and the common scorer, at 100 games per arm\. Only the configuration bundle varied\. Two features of the design bound its interpretation\. First, the arms ran*back\-to\-back on one day*rather than randomised or interleaved, so residual intra\-window serving variation cannot be excluded\. Second, H and R differ as a bundle of six components, not as a manipulated factor: the transport \(an OpenAI\-compatible endpoint versus the provider’s native API\), the elicitation mode \(a combined move\-and\-belief call versus two separate calls\), the presentation of the model’s own state, the thinking setting \(none versus a fixed medium level\), whether sampling parameters are forwarded, and the revision of the rules document supplied in the prompt\. Under the reporting scheme used here, the H/R bundle crosses both the*measurement\-instrument*and*inference\-configuration*coordinates of Section[9](https://arxiv.org/html/2609.22478#S9): transport, elicitation mode, own\-state presentation and the rules\-document revision belong to the instrument, while the thinking setting and sampling\-parameter forwarding belong to the inference configuration\. That grouping is an operational classification applied after the fact, not a decomposition of the treatment; all six components varied jointly\. The consequence for inference is that the endpoint difference is*associated with the evaluation and inference configuration bundle as a whole*: neither an individual component nor either coordinate’s sub\-bundle is isolated by this design, and we do not attribute the shift to any one of them\.

#### What the rules\-document component is not\.

The last component in that bundle could be mistaken for a change in the game, so we state what it is: the two rules\-document revisions differ only in a trailing version block and contain no differing normative text, so the gameplay rules were identical across the arms\.

#### The core grid\.

The persistence question is addressed by a2×22\\times 2factorial crossing two Gemini identifiers with two generated\-token ceilings, at 150 games per cell: cells A and B are Gemini 3\.1 Flash\-Lite at the 4,096\- and 16,384\-token ceilings, and cells C and D are Gemini 3\.7 Flash at the same two ceilings\. The opponent, environment seeds, elicitation architecture, scoring rules, and stopping criteria are fixed across all four cells\. Two exploratory cells, E and F, extend the design to Gemini 3\.8 Flash — an identifier released during execution of the core grid — at the same two ceilings\.

The provenance of these cells is not uniform, and the differences change what each one can support\. Cell D was executed first: it ran in the immediately preceding serving window and completed before the A/B/C interleaved window opened, and it is what motivated building the grid\. Its outcome therefore preceded the freeze of the classification rule, so its label is descriptive and is not prospectively confirmatory\. Cells A, B, and C, together with the classification rule itself, were frozen and sealed before any of their scientific outcomes were known, and the three ran on interleaved schedules within one serving window\. The strongest prospective cross\-identifier comparison available is thereforeA versus C: the same output ceiling, the same rebuilt configuration, both prospectively frozen, and interleaved execution\. Comparisons involving D cross serving windows and are reported as such\. The Gemini 3\.8 extension was initially frozen at 150 games per cell before any call to that identifier; after E’s first 75\-game block completed, only prespecified operational information — runtime, cost, transport behaviour, and output\-ceiling pressure — was inspected, and on that basis alone, before cell F began, the design was amended to 75 games per cell and downgraded to exploratory\. No scientific endpoint, belief content, or correctness signal from either cell was inspected at that point\. E therefore ran under the original confirmatory plan and F entirely under the amended exploratory one, and neither carries confirmatory weight anywhere in this paper\.

One confound in the grid cannot be removed by design and is stated wherever the comparison appears\. Gemini 3\.1 Flash\-Lite and Gemini 3\.7/3\.8 Flash differ in release*and*in product tier, with whatever difference in served capacity that entails\. The design randomises neither, nor the trajectory distribution each identifier induces through its own play\. Every cross\-identifier statement in this paper is therefore a statement about*tested identifiers*, not about an isolated model version\.

#### The opponent\.

All interactive conditions used the same fixed heuristic opponent, referred to throughout as Tier\-1, at its medium setting: static one\-ply move evaluation with stochastic selection among its top three scored moves\. The label denotes a configuration, not an externally calibrated chess\-strength level, and it was fixed before any condition’s results were known\. Its Crown\-Shift policy is relevant to how predictable the hidden state is: it shifts when its own Regent is attacked, and otherwise at a per\-game first\-shift move drawn uniformly from moves 4–12 and thereafter with 15% probability per turn, choosing the target by a deterministic safety heuristic that favours unattacked, well\-defended, non\-central, and less conspicuous pieces\. Hidden\-state timing is thus only partly state\-responsive, which bounds how far the latent state can be predicted from public play at all — a bound that applies to any predictor, including the reference tracker discussed in Section[8](https://arxiv.org/html/2609.22478#S8)\. Opportunity density for the actionability analysis is likewise opponent\-dependent, so results characterise this fixed regime rather than an opponent\-invariant property of a model\.

#### Cross\-family transport\.

One condition sits outside the factorial and outside its classification scheme\. A prospectively frozen cross\-family transport tests whether the reversal is confined to the Gemini lineage: GPT\-5\.6, accessed as the transport identifier “Terra” over a different provider API at the 16,384\-token ceiling, with the same fixed opponent, the same elicitation architecture, and the same 75 environment seeds as cell F\. Its sample size was fixed prospectively rather than by an outcome\-dependent stopping rule\. It is not simply another R cell: it preserves R’s elicitation architecture over a provider\-specific implementation with its own request shaping and reasoning configuration, so it is transport\-analogous to R rather than transport\-identical, and we report it separately and never under the factorial’s classification labels\.

#### Statistical and provenance conventions\.

Endpoints, cutoffs, and the classification rule were frozen before the conditions they judge, and every condition carries an explicit status: confirmatory where it was prospectively frozen, descriptive where its outcome preceded the relevant freeze, and exploratory where it was downgraded on operational grounds\. All confidence intervals are game\-clustered bootstrap intervals, because many named\-candidate events occur within a single game and are not independent; resampling is therefore at the level of whole games, with the number of replicates and the seed fixed in advance\. Analyses whose specification postdates the results they describe — the depth and state\-richness stratifications, and the actionability decomposition — are labelled as such at every point of use, and cross\-cell contrasts are exploratory relative to the frozen design, which ran no cross\-cell test\. Where a stratified analysis has fewer than 100 contributing game clusters, it is reported descriptively rather than inferentially under the study’s existing support convention\. Finally, every reported quantity was recomputed by independent reimplementations that share no scoring code with the canonical pipeline and were built from the frozen endpoint definitions alone; all quantities reported in this paper derive from a frozen, independently audited result set\. Per\-condition game counts, identifiers, freeze sequence, and the integrity record are in Appendices[A\.5](https://arxiv.org/html/2609.22478#A1.SS5),[A\.6](https://arxiv.org/html/2609.22478#A1.SS6)and[A\.12](https://arxiv.org/html/2609.22478#A1.SS12)\. Figure[2](https://arxiv.org/html/2609.22478#S4.F2)summarises the three questions, what each contrast holds fixed and varies, what each therefore licenses, and the execution and freeze order that the following sections rely on\.

Figure 2:Three validation questions and the contrasts that answer them\.Row 2’s*Varied*cell shows the H/R bundle as a single treatment: all six components varied together, bracketed as one unit and grouped below only by reporting coordinate \(four measurement\-instrument, two inference\-configuration\), so the contrast spans both coordinates of the scheme in Section[9](https://arxiv.org/html/2609.22478#S9)\. That grouping is operational, not a decomposition: neither a component nor either sub\-bundle is identified\. Row 3 records that identifier comparisons do not share a common design/provenance status\. Cell D’s outcome preceded the rule freeze, so its label is descriptive\.

## 5Replication and Measurement Sensitivity

This section answers two of the three questions, and keeps them apart\. The first asks whether the historical finding recurs on newly generated games when its own configuration is rerun\. The second asks how much the endpoint moves when the configuration is rebuilt with the model identifier and the serving day held fixed\. Persistence across identifiers is a separate question and is deferred to Section[6](https://arxiv.org/html/2609.22478#S6)\.

#### Fresh\-data replication under the historical configuration\.

Rerunning H in a later serving period, on newly generated games, recovers the historical result\. The historical 60\-game arm — the reference arm for this comparison, because it is the larger of the two historical runs and the only one this contrast uses — givesΔR​1=\+0\.0696\\Delta\_\{R1\}=\+0\.0696, 95% CI\[\+0\.0428,\+0\.0937\]\[\+0\.0428,\+0\.0937\]\. The rerun \(“H\-current”, 100 games, 2,444 named\-candidate events across 94 scoreable games\) gives\+0\.0530\+0\.0530,\[\+0\.0329,\+0\.0714\]\[\+0\.0329,\+0\.0714\]\. Both intervals lie entirely above zero, so both receive the frozen endpoint\-status labelreplicates: the model scores worse than its matched comparator, in the direction the historical degradation had\. The label is doing only that work\. The study\-design claim is the separate one, and it is stronger than the label: new games were generated under the historical configuration, so this is a*fresh\-data replication under H*\. The 20\-game historical arm \(\+0\.0593\+0\.0593,\[\+0\.0292,\+0\.0931\]\[\+0\.0292,\+0\.0931\]\) is reported as descriptive sensitivity only and is never pooled with the 60\-game arm\.

The contrast between them — H\-current minus the historical 60\-game arm — is−0\.0166\-0\.0166, 95% CI\[−0\.0483,\+0\.0157\]\[\-0\.0483,\+0\.0157\], which spans zero\. This is the comparison that would speak to a serving\-period contribution, and it is inconclusive\. The inconclusiveness is a statement about precision rather than about the effect: the historical arm is fixed at 60 games, so the interval’s half\-width cannot fall below0\.02540\.0254however much new data is collected, and the realised half\-width is0\.03200\.0320\. Reading this interval as evidence of equivalence, or as evidence of no serving\-period effect, would be a mistake in both directions\.

Format\-level behaviour was not identical across the two windows even under H, and reporting it is part of reporting the replication honestly\. Well\-formed elicitation ran at 82\.3% in the archived historical arm against 72\.1% \(1,212 of 1,682\) in H\-current, a difference of−10\.3\-10\.3percentage points, inside the prospectively frozen±15\\pm 15\-point diagnostic band\. That records a difference in format\-level behaviour across windows under one configuration\. It is not evidence of a mechanism, and not evidence of a backend change\.

The reconstructed Gemini 3\.1 conditions under R, reported in Section[6](https://arxiv.org/html/2609.22478#S6), recover the same degradation direction but at materially attenuated magnitude — roughly one\-third to one\-half that of the historical references, at both the 4K and 16K ceilings\. That attenuation is descriptive\. The reconstructed and historical conditions differ in measurement configuration and serving period at once, so it isolates no configuration component, no serving\-period contribution, and no other cause; it is the reason for the control described next\.

#### Measurement sensitivity: H\-current versus R\-current\.

Both arms ran in the same serving window, under the same public model identifier, with output ceiling, opponent, game horizon, seed schedule, colour balance, and scorer held fixed, at 100 games each \(Section[4](https://arxiv.org/html/2609.22478#S4)\)\. Under H the deficit is\+0\.0530\+0\.0530,\[\+0\.0329,\+0\.0714\]\[\+0\.0329,\+0\.0714\]\(replicates\)\. Under R, in the same window, it is\+0\.0101\+0\.0101,\[−0\.0036,\+0\.0234\]\[\-0\.0036,\+0\.0234\], whose interval spans zero \(unresolved\)\. The H−\-R contrast isΔ=\+0\.0429\\Delta=\+0\.0429, 95% CI\[\+0\.0182,\+0\.0667\]\[\+0\.0182,\+0\.0667\], entirely above zero\. The shared environment\-seed schedule equalises the opponent’s randomisation across arms but does not produce matched games, so the two arms are analysed unpaired, with resampling clustered on whole games\. Integrity was complete on both arms: 100 of 100 games on the frozen seed schedule, no errored games, no game reaching the 150\-ply horizon, no truncated generations, and every configuration field single\-valued within its arm\.

Well\-formedness was also not identical across the two configurations, and because responses that are not well formed are excluded rather than mended, each arm is scored on its own eligible population\. A configuration\-dependent change in which outputs are well formed enough to enter the endpoint is itself part of the observed measurement sensitivity; consequently the H−\-R contrast characterises the complete measurement endpoint, including the scoreable population that endpoint induces, rather than belief quality on a fixed common subset\.

What the control establishes is a*material endpoint difference associated with the bundled evaluation and inference configuration*, measured under one public identifier on one day, subject in full to the design qualifications set out in Section[4](https://arxiv.org/html/2609.22478#S4)\. Two consequences of those qualifications matter for reading the number\. The difference is an association with the bundle, not a demonstration that the bundle produced the historical result: we do not claim it explains the historical gap, and the historical\-versus\-reconstructed difference itself remains jointly indexed by configuration and serving period\. And the comparison speaks to this identifier on this day, not to configuration sensitivity in general\.

#### R\-current beside cell A\.

Under R the deficit is directionally positive both in this control arm \(\+0\.0101\+0\.0101,\[−0\.0036,\+0\.0234\]\[\-0\.0036,\+0\.0234\], 97 scoreable games of 100\) and in cell A of the grid below, which shares the tested identifier, the rebuilt configuration R and the 4K ceiling \(\+0\.0242\+0\.0242,\[\+0\.0108,\+0\.0363\]\[\+0\.0108,\+0\.0363\], 145 scoreable games of 150\)\. The control arm’s interval spans zero and is labelledunresolved; cell A’s does not and is labelledreplicates\. The two intervals overlap, the point estimates differ, and the two executions ran in different serving windows at different sample sizes under no predeclared contrast\. The differing frozen labels are therefore not evidence of a serving\-period effect, of a sample\-size effect, or of any other isolated cause; they are two separate executions whose classification rule happened to fall on opposite sides of zero\. Figure[3](https://arxiv.org/html/2609.22478#S5.F3)places every condition in the study on the one primary\-endpoint scale, with each row’s design status and, where the design confers one, its frozen endpoint status\.

Figure 3:Primary endpointΔR​1\\Delta\_\{R1\}across every condition in the study\.Intervals are game\-clustered 95% bootstrap intervals at the canonical board\-ply≥8\\geq 8cutoff\.*Two different kinds of status are shown on two separate channels and must not be conflated:*the marker gives each row’s design and inferential status, the right\-hand column the frozen endpoint status where the design confers one\. Groups are distinct study designs that share an endpoint scale; co\-location does not license arbitrary cross\-group contrasts\. Aggregate R1 is support\-dependent: scalarΔR​1\\Delta\_\{R1\}magnitudes are conditional on model\-selected support and are not global belief\-quality comparisons, so the plot reads by sign and interval position relative to zero and by endpoint\-status pattern, not by scalar distance\.‡\\ddaggerR\-current and cell A are distinct executions under the same identifier, configuration R and 4K ceiling, run in separate serving windows at different sample sizes; their intervals overlap and no predeclared contrast relates them — the marker explains why two closely related executions carry different frozen labels, and implies neither a paired nor a controlled comparison, nor a serving\-period or sample\-size explanation\.†\\daggerCell D’scontradictsis a sign classification only; the cell is descriptive, its outcome having preceded the rule freeze\. Cells E and F are exploratory and carry no factorial endpoint label\. The cross\-family transport is a separate protocol reported outside the factorial status scheme\. The archived 20\-game historical arm is shown as descriptive historical sensitivity context and is not the historical reference arm\.Read together, the two halves of this section already make the paper’s narrower methodological point\. The same nominal model, measured in the same window through two configurations of the same nominal evaluation, produces endpoints one of which is labelledreplicatesand one of which isunresolved\. Whatever else is true of the finding, a report of it that names only the model is not a report of a reproducible measurement\.

## 6Persistence Under the Rebuilt Instrument

The persistence question is asked under a single common instrument, so that a difference between identifiers cannot be a difference between harnesses\. All six cells below were evaluated under the rebuilt configuration R\.

#### The core grid\.

Table[1](https://arxiv.org/html/2609.22478#S6.T1)reports all six cells\. The originally tested identifier retains the deficit at both ceilings: cell A \(Gemini 3\.1 Flash\-Lite, 4K\) gives\+0\.0242\+0\.0242,\[\+0\.0108,\+0\.0363\]\[\+0\.0108,\+0\.0363\]over 6,611 events in 145 scoreable games, and cell B \(16K\) gives\+0\.0262\+0\.0262,\[\+0\.0133,\+0\.0384\]\[\+0\.0133,\+0\.0384\]over 6,687 events in 147 games\. Both arereplicates\. The next identifier tested reverses the endpoint direction at both ceilings: cell C \(Gemini 3\.7 Flash, 4K\) gives−0\.0131\-0\.0131,\[−0\.0155,−0\.0108\]\[\-0\.0155,\-0\.0108\]over 21,550 events in 150 games, and cell D \(16K\) gives−0\.0104\-0\.0104,\[−0\.0130,−0\.0079\]\[\-0\.0130,\-0\.0079\]over 21,498 events in 150 games\. Both arecontradicts, and the sign classification is therefore unchanged across the two tested ceilings within each identifier\.

Table 1:Core grid, all six cells, under the common rebuilt configuration\.R1 is the primary endpoint; positive means worse than the matched comparator, negative better\. Classification is the frozen interval\-versus\-zero rule of Section[2](https://arxiv.org/html/2609.22478#S2), and is an endpoint\-status label\. Cell D’s label is descriptive: its outcome preceded the freeze of that rule\. Cells E and F are exploratory and carry no classification\. The cross\-family transport is reported in the text, not here, because it sits outside this design and its classification scheme\.†Descriptive only\. Cell D ran in the immediately preceding serving window and completed before the A/B/C interleaved window opened; its outcome therefore preceded the rule freeze and it is not prospectively confirmatory\.

Not all four cells support the same inference, and the asymmetry is a property of when they ran rather than of what they measured\.A versus C is the strongest cross\-identifier comparison available: one common output ceiling, one common configuration, both cells prospectively frozen, and interleaved execution within one serving window\.B versus D is interpretively weakeron one specific ground — D ran in the immediately preceding serving window and completed before the A/B/C interleaved window opened, so any B\-versus\-D contrast crosses serving windows, which is exactly the confound the same\-window control of Section[5](https://arxiv.org/html/2609.22478#S5)exists to bound\. For completeness the cross\-identifier contrasts are\+0\.0373\+0\.0373,\[\+0\.0233,\+0\.0498\]\[\+0\.0233,\+0\.0498\]at 4K \(A versus C\) and\+0\.0367\+0\.0367,\[\+0\.0236,\+0\.0492\]\[\+0\.0236,\+0\.0492\]at 16K \(B versus D\); both are exploratory relative to the frozen design, which specified no cross\-cell test\. And whichever pairing is used, the two identifiers differ in release*and*in product tier, neither of which this design randomises, so what the grid contrasts is tested identifiers\.

#### Exploratory extension to a third identifier\.

Cells E and F extend the design, under the same configuration R, to Gemini 3\.8 Flash — an identifier released during execution of the core grid\. Both fall on the same side of the comparator as the Gemini 3\.7 cells, at both ceilings \(−0\.0136\-0\.0136at 4K,−0\.0126\-0\.0126at 16K\), so the reversal is not confined to a single tested release\. These two cells were downgraded to exploratory on operational grounds before either was scored, as described in Section[4](https://arxiv.org/html/2609.22478#S4), and they carry no confirmatory weight anywhere in this paper: they show a pattern is not isolated, and nothing stronger\.

#### What the two ceilings do and do not establish\.

Belief generation did not bind the tested ceilings in any core cell: belief\-call truncation was zero in all four of A, B, C and D\. The grid therefore establishes that the sign classification is*invariant over the tested non\-binding ceilings*— which is a statement about robustness of the endpoint to a parameter that never became active, not an estimate of a token\-budget effect\. No isolated token\-budget effect is claimed or estimable here\. One exploratory cell does speak to the question from the other side: in cell E the 4K ceiling genuinely bound, truncating 24\.3% \(384 of 1,580\) of belief calls, and the cell still landed on the negative side of the comparator\. That weighs against a pure truncation account of the reversal without estimating a causal effect of truncation, and cell F at 16K, where nothing truncated, lands in the same place\.

#### Cross\-family transport\.

The reversal is not confined to one provider lineage\. A prospectively frozen cross\-family transport — GPT\-5\.6, accessed as the transport identifier “Terra” over a different provider API, at the 16K ceiling, with the same fixed opponent, the same elicitation architecture and the same 75 environment seeds as cell F — givesΔR​1=−0\.0069\\Delta\_\{R1\}=\-0\.0069, 95% CI\[−0\.0106,−0\.0032\]\[\-0\.0106,\-0\.0032\]over 9,873 events in 75 games, on the opposite side of the comparator from the historical degradation\. Two things about its status are deliberate\. It is reported outside the factorial and outside the factorial’s classification scheme, which is reserved for the Gemini reconstruction design, so it carries the protocol’s own descriptive label rather thanreplicatesorcontradicts\. And it is not simply another R cell: it preserves R’s elicitation architecture over a provider\-specific implementation with its own request shaping and reasoning configuration, which makes it transport\-analogous to R rather than transport\-identical\. Its sample size was fixed prospectively rather than by an outcome\-dependent stopping rule\. Terra is the only cross\-family transport tested, and its difference attenuates under stricter depth restrictions \(Section[8](https://arxiv.org/html/2609.22478#S8)\)\.

## 7Behavioural Decomposition

Figure 4:Opportunity\-conditioned stages, split at the denominator change\.\(a\)Represented \(named at all\), top\-ranked, andp≥0\.5p\\geq 0\.5share one denominator — usable\-belief opportunity plies — so the three stages are connected\.\(b\)Conversion is conditional on the opportunities that reachedp≥0\.5p\\geq 0\.5, a different and much smaller population, so each condition’snnis given in the legend and no line joins it to \(a\)\. Circles mark the 4K and squares the 16K output ceiling; the exploratory Gemini 3\.8 series are hollow and dashed; the cross\-family transport is the triangle\. All values are read from the corrected opportunity artifact\. The figure is descriptive and identifies no mechanism\.A secondary analysis conditions on actionability, which neither R1 nor R2 does\. An*opportunity*exists on one of the model’s own turns when the opponent’s true Regent is among its legal capture targets in the exact pre\-move position; capturing it wins immediately, so both the availability of the action and its relevance are unambiguous\. Figure[4](https://arxiv.org/html/2609.22478#S7.F4)decomposes belief quality on that population into four stages for all six cells, the historical corpus, and the cross\-family transport\. In the newer conditions \(C through F\) the true hidden state is*represented*— named as a candidate at all — on 97\.9–100% of usable\-belief opportunity plies, but is*top\-ranked*on only 28\.1–34\.7% of them and assignedp≥0\.5p\\geq 0\.5on only 16\.3–22\.4%\. Once that confidence threshold is reached the available win is usually taken: 65 of 70 such opportunities in cell C, 57 of 63 in D, 34 of 38 in E, 25 of 32 in F, and 23 of 29 under the cross\-family transport\. The historical corpus sits far below on the first stage, with the true state represented on 41\.2% of its usable\-belief opportunity plies, top\-ranked on 17\.6%, and atp≥0\.5p\\geq 0\.5on 17\.6%, converting 1 of 6\. Coverage of the hidden state, in short, saturates before concentration on it does\.

Three limits bound what that pattern can mean\. First, it identifies no mechanism\. The staged gap between representation and confidence co\-varies with tested identifier, and this analysis does not establish why: it is compatible with better hidden\-state tracking, with more selective assignment of high confidence, or with both, and nothing here separates them\. We therefore do not claim that the later identifiers learned to track the hidden state, that tracking causally improved, or that tracking has been distinguished from confidence calibration\. Second, the analysis is ancillary and descriptive throughout — it introduces no inferential test, does not modify R1 or R2, and its provenance differs by condition: the historical corpus and cells A–D were scored post\-hoc under a specification written after those results existed, the E/F specification was frozen before scientific unseal though not prospective in the strong sense the core endpoints were, and the transport’s opportunity analysis was prospectively frozen before execution\. Third, the population is opponent\-dependent\. Opportunity density is a property of the fixed opponent’s play, so these rates characterise that regime rather than an opponent\-invariant property of a model, and the high whole\-game win rates in the newer conditions \(98\.7–100%, and 89\.3% for the transport\) are consistent with the staged gap rather than in tension with it: a game needs one terminal capture, while a trajectory can contain many actionable opportunities\. Full cross\-tabulations, denominators, and the en\-passant implementation correction that fixes the opportunity denominators are in Appendix[A\.11](https://arxiv.org/html/2609.22478#A1.SS11)\.

## 8Comparator and Robustness Context

Four things materially constrain how the endpoints above may be read, and this section states them compactly rather than re\-deriving them\.

#### Support dependence, and what R2 adds\.

R1’s aggregate is support\-dependent because the model selects its own event set \(Section[2](https://arxiv.org/html/2609.22478#S2)\), and the tested identifiers differ materially on exactly that axis: 4\.50 and 4\.48 named candidates per scored ply in cells A and B, against 8\.39 and 8\.68 in C and D, and 8\.32 for the cross\-family transport measured over its eligible belief plies\. R2, the complementary endpoint, scores the full elicited partition including the residual, so it also penalises leaving the true state unnamed:\+0\.0575\+0\.0575\[−0\.0413,\+0\.1509\]\[\-0\.0413,\+0\.1509\]in A,\+0\.1473\+0\.1473\[\+0\.0493,\+0\.2392\]\[\+0\.0493,\+0\.2392\]in B,−0\.1199\-0\.1199\[−0\.1416,−0\.0979\]\[\-0\.1416,\-0\.0979\]in C,−0\.1028\-0\.1028\[−0\.1269,−0\.0783\]\[\-0\.1269,\-0\.0783\]in D, and−0\.1307\-0\.1307and−0\.1233\-0\.1233in the exploratory E and F\. R2 moves with R1 in three of the four core cells; cell A’s canonical interval includes zero, and we report that rather than reading the point estimate alone\. R2 magnitudes are support\-dependent in the same way as R1’s\. The residual itself is where much of the difference sits: the true state falls in the unnamed residual on 23\.0% and 30\.8% of scored plies in A and B, against 1\.5% and 1\.1% in C and D, and 1\.77% for the transport over its diagnostics population\.

#### Depth and state richness\.

Both identifier groups were re\-scored at two stricter prespecified depth cutoffs\. The Gemini 3\.1 cells strengthen monotonically with depth \(A rises to\+0\.0411\+0\.0411at ply≥10\\geq 10and\+0\.0618\+0\.0618at ply≥14\\geq 14; B to\+0\.0442\+0\.0442and\+0\.0703\+0\.0703\), while every Gemini 3\.7 and 3\.8 condition shrinks toward zero, with cell C the only one retaining an interval entirely below zero at ply≥14\\geq 14\(−0\.0053\-0\.0053,\[−0\.0077,−0\.0029\]\[\-0\.0077,\-0\.0029\]\) and cell D crossing intounresolvedthere\. The transport shows the same shrinking signature, approximately zero by ply≥14\\geq 14\. This is a descriptive re\-analysis, not a preregistered interaction test, and no cutoff revises any condition’s canonical classification\. A separate exploratory stratification asks whether the reversal is an artifact of late\-game candidate\-set collapse by restricting scoring to plies with at least eight live opponent pieces — over 80% of eligible events in each core cell\. It is not: the cross\-identifier difference persists there at both ceilings,\+0\.0277\+0\.0277\[\+0\.0128,\+0\.0414\]\[\+0\.0128,\+0\.0414\]at 4K and\+0\.0310\+0\.0310\[\+0\.0172,\+0\.0446\]\[\+0\.0172,\+0\.0446\]at 16K, modestly attenuated relative to the all\-support contrasts \(Appendix[A\.3](https://arxiv.org/html/2609.22478#A1.SS3)\)\. The two exploratory cells fall below the study’s 100\-cluster support floor in that stratum and are reported descriptively, outside the inferential claim\.

#### The capture\-time diagnostic\.

A separate diagnostic scores only the captured\-square event, as the ratio of model to matched\-uniform Brier loss\. It falls from roughly4\.24\.2–4\.6×4\.6\\timesthe comparator for Gemini 3\.1 Flash\-Lite to approximately parity for Gemini 3\.7 Flash \(0\.970\.97–0\.99×0\.99\\times\)\. This is a different population from the primary endpoints and from the transport’s own capture diagnostic, and the three should not be placed on one axis\. Improvement to parity is not resolution: at the 16K ceiling the absolute R2 loss is still0\.73750\.7375against the matched comparator’s0\.84030\.8403, so substantial absolute error persists in the improved conditions\.

#### How weak is the matched comparator?

A uniform prior over live opponent pieces is a deliberately undemanding benchmark, and it is fair to ask whether beating it or losing to it means much\. One piece of context bounds the answer on this population\. A predecessor study built an auxiliary tracker that updates a distribution over which opponent piece holds royal status using only deductively valid rules keyed to publicly observable events \(Appendix[A\.9](https://arxiv.org/html/2609.22478#A1.SS9)\)\. Scored against matched uniform on the historical capture\-only population at board ply≥8\\geq 8, it showed only a small advantage in one historical batch \(n=77n=77\) and no clear advantage in the other \(n=220n=220\)\. We therefore use it only as limited\-headroom context, and not as a stronger comparator, not as a tractability certificate, and not as evidence that the hidden state is predictable after a shift\. Its own scope is narrow on three axes at once — one tracker design, one opponent, one historical population — and the opponent’s shift timing is only partly state\-responsive by policy \(Section[4](https://arxiv.org/html/2609.22478#S4)\), which bounds what any public\-information predictor could achieve here\.

## 9Discussion and Scope

The results support a narrow claim precisely, and the boundaries below are the conditions under which that claim holds rather than a list of shortcomings\. Stating them as scope is the honest framing: each one is a choice the design made, and most of them could only be relaxed by a different study\.

What the results establish is that three validation questions about one behavioural finding can dissociate\. Rerunning the historical measurement configuration on newly generated games recovers the finding\. Substituting a rebuilt configuration within one day and under one public identifier moves the endpoint materially\. And under that common rebuilt configuration, the finding does not carry over to the next identifiers tested\. No one of those three statements implies either of the others, which is the point\.

#### Scope conditions\.

The boundaries below group into four kinds\.

- •Environment and opponent\.All results come from one controlled sequential hidden\-state environment, chosen because it records latent truth exactly, and every interactive condition faced one fixed Tier\-1 heuristic opponent\. Trajectory distributions, opportunity density, and how far the hidden state is predictable from public play are therefore properties of that regime rather than of the models; whether the dissociation appears in other action\-time settings is untested here\.
- •Identifier and provider\.The tested Gemini identifiers differ in release*and*product tier, neither of which is randomised, so every cross\-identifier statement is about tested identifiers rather than an isolated version effect \(Section[6](https://arxiv.org/html/2609.22478#S6)\)\. The later identifiers were evaluated under R only, so persistence here means persistence under the common rebuilt instrument, not across instruments\. One cross\-family transport shows the reversal is not confined to a single provider lineage, which is not provider\-level generality\.
- •H/R design\.The configuration control varies a six\-component bundle in one same\-day, back\-to\-back comparison \(Section[4](https://arxiv.org/html/2609.22478#S4)\)\. It bounds the configuration question as a whole and resolves no component within it, and the serving\-period contribution remains unresolved at a precision the fixed historical sample size bounds from below — neither an effect nor an equivalence\.
- •Measurement and provenance\.R1’s aggregate remains support\-dependent because the model selects its own event set \(Section[2](https://arxiv.org/html/2609.22478#S2)\), so the confirmatory design rests on sign and classification rather than magnitude\. And no mechanism is identified: nothing here explains why the later identifiers differ — not serving\-side change, not the output ceiling, and not the gap between representing the hidden state and concentrating probability on it\.

#### An asymmetry in endpoint\-identity verification\.

One provenance gap deserves stating in its own right\. Only the Gemini 3\.8 identifier received an explicit provider metadata\-resolution audit, in which the provider\-returned resolved version string was recorded and carried no preview or experimental marker\. No equivalent resolved\-version audit exists for the other two Gemini identifiers in any execution window, including the historical runs and their reconstruction\. This is an asymmetry in how firmly the served endpoint behind each identifier was verified, not evidence that any identifier resolved to something unexpected: nothing here indicates that the unaudited identifiers were wrong, only that we cannot demonstrate from our own records what they resolved to\. It is also exactly the condition under which this paper’s own argument applies to itself — an identifier without a resolution record is a weaker provenance claim than one with it\.

#### Why the three questions should not be collapsed\.

They differ in what is held fixed and therefore in what a result can license\.*Replication*holds the measurement configuration fixed and varies the data, answering whether the finding recurs\.*Measurement sensitivity*holds the identifier and serving period fixed and varies the configuration, answering whether the finding is a property of the measurement\.*Persistence*holds the configuration fixed and varies the tested identifier, answering whether the finding still describes what is being served now\. Reporting a single rerun answers at most one of them while appearing to answer all three: a successful rerun under the original harness says nothing about the next release, and a failed rerun under a rebuilt harness cannot distinguish a changed model from a changed instrument\. That is not a hypothetical concern in this study\. The same identifier, in the same window, measured through two configurations, produced one endpoint labelledreplicatesand one labelledunresolved\.

#### Methodological implication\.

A hosted\-model behavioural claim should be indexed to four things, not one: the*tested identifier*, the*serving period*in which it was measured, the*measurement instrument*that elicited and scored the behaviour, and the*inference configuration*under which the model was run\. A claim indexed only to a model name is not wrong so much as incomplete — it does not say enough for anyone, including its own authors, to know what a subsequent rerun is comparing itself to\. The design artefacts here are reusable in a way a single measured outcome is not: a frozen elicitation architecture, frozen endpoints, and a frozen actionability definition can be applied to any future release at known marginal cost, whereas the measured outcome may already describe a service that is no longer being served\.

## 10Related Work

Calibration and probabilistic belief elicitation\.Work on confidence and calibration in language models has largely evaluated probabilities in static settings, where the model answers a question or labels an instance and reports confidence in that same act\([Kadavath et al\., 2022](https://arxiv.org/html/2609.22478#bib.bib5);[Kim & Kang, 2026](https://arxiv.org/html/2609.22478#bib.bib7);[Li et al\., 2025](https://arxiv.org/html/2609.22478#bib.bib10);[Wang & Stengel\-Eskin, 2026](https://arxiv.org/html/2609.22478#bib.bib16);[Leng et al\., 2025](https://arxiv.org/html/2609.22478#bib.bib8);[ffrench\-Constant et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib2)\)\. That literature establishes the phenomena we rely on — that calibration is often poor, that overconfidence is systematic, and that calibration quality varies sharply across families and versions — and one such benchmark independently places the model at the centre of this study at the poor end of its own calibration distribution on an unrelated task family\([ffrench\-Constant et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib2)\)\. What that design cannot separate is the scored answer from the stated confidence, because they are the same output\. We move the measurement into a sequential interactive setting and elicit belief about an already\-determined hidden state in a call separate from the one that chooses the action, which makes belief quality and action quality separately scoreable\.

Interactive and hidden\-state evaluation\.Competitive\-game platforms\([Olszewska & Risdal, 2025](https://arxiv.org/html/2609.22478#bib.bib12)\)and agent benchmarks under partial observability\([Singh et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib14);[Samanta et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib13)\), together with social\-deduction settings built to probe hidden\-role inference\([Agarwal et al\., 2025](https://arxiv.org/html/2609.22478#bib.bib1);[Karpov, 2026](https://arxiv.org/html/2609.22478#bib.bib6)\), increasingly place models where latent state must be inferred from interaction history\. Most score task success or action quality; where belief is elicited at all, it is typically optimised against downstream reward rather than scored against the action it informed\. The environment used here contributes exactly recoverable hidden\-state ground truth together with explicit probability elicitation, which is what permits a proper score at the moment of action\.

Hosted\-endpoint temporal and configuration variability\.A longitudinal study tracking GPT models on materials\-science tasks over 18 months reports 9–43% performance variation, attributes part of it to silent endpoint updates and version swaps, and recommends recording exact version strings and evaluation dates\([Venugopal et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib15)\)\. A supply\-side measurement study makes a structurally related point from the provider side: a hosted model identifier names a provider\-specific, time\-varying service rather than a fixed artefact\([Li et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib9)\)\. Separately, static factuality benchmarks age as the facts they test become outdated\([Jiang et al\., 2026](https://arxiv.org/html/2609.22478#bib.bib3)\)— the converse mechanism, in which benchmark content drifts relative to the world rather than the service drifting relative to a fixed evaluation\. Our contribution here is the instrument dimension these accounts do not isolate: reconstructing the measurement configuration is itself a source of measurement difference, and it is separable from serving period by design rather than by argument\.

Reproducibility and replication methodology\.We use the standard distinction between recovering reported results from archived artifacts and conducting a fresh study on newly generated data\([National Academies of Sciences, Engineering, and Medicine, 2019](https://arxiv.org/html/2609.22478#bib.bib11)\), and we keep it visible in the results themselves rather than confining it to terminology: the historical rerun is a fresh\-data replication, while the factorial cells are evaluations under a rebuilt configuration and are never described as replications of the historical experiment\.

What is and is not new here\.We do not claim to discover that hosted APIs vary over time, nor that measurement details matter; both are established, and the studies above say so\. The contribution is evidential and specific: using action\-time proper scoring against exactly recorded hidden\-state ground truth, we show that fresh\-data replication, across\-identifier persistence, and measurement\-configuration sensitivity can*dissociate within a single behavioural evaluation*— the same finding replicating under its own instrument, moving materially when the instrument is rebuilt under one identifier on one day, and failing to persist across the next identifiers tested under that common instrument\. The accompanying elicitation analysis is a second, smaller contribution of the same kind: it shows that the format in which belief is elicited is not a neutral implementation choice, measured against prospectively frozen decision rules rather than asserted\.

## 11Conclusion

Rerun on newly generated games under its own historical measurement configuration, the previously reported action\-time belief deficit recovers: the endpoint remains on the same side of its matched comparator, with the frozen classification unchanged\. Substituting a rebuilt measurement configuration in the same serving window and under the same public model identifier moves that endpoint materially, by an amount comparable to the deficit itself, and the design associates the shift with the configuration bundle as a whole rather than with any component of it\. Under that common rebuilt configuration the deficit then fails to persist: the next Gemini identifier tested reverses the endpoint direction at both tested output ceilings, as does a further exploratory release and a cross\-family transport\.

The behavioural decomposition adds a specific shape to the improvement rather than a mechanism for it\. On states where the hidden target was legally actionable, the newer conditions represent the true state almost whenever they can, while ranking it first or assigning it majority probability far less often — coverage saturates before concentration does\. That pattern is compatible with better tracking, with more selective confidence, or with both, and this study does not separate them\.

What follows for practice is a reporting discipline rather than a correction to any particular result\. A behavioural claim about a hosted model should be indexed to the tested identifier, the serving period, the measurement instrument, and the inference configuration, because a rerun that shares only the model name is not necessarily measuring the same object\. Reversal is also not resolution: substantial absolute error persists in the improved conditions, and nothing here establishes why the transition occurred or whether it will hold in the next release tested\.

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## Appendix AAppendix

This appendix provides the full detail supporting the main text\. No claim in Sections[1](https://arxiv.org/html/2609.22478#S1)–[11](https://arxiv.org/html/2609.22478#S11)depends on the reader consulting it\. It is written to be audited rather than read continuously: definitions are given exactly, every table carries its own population and status, and interpretation is confined to short notes attached to the quantity being interpreted\. All reported quantities derive from a frozen, independently audited result set\.

### A\.1Full environment rules

Condensed from the predecessor study that introduced the environment\([Joshi, 2026](https://arxiv.org/html/2609.22478#bib.bib4)\); platform, interface and data\-consent provisions that do not affect the reported game mechanics are omitted\.

Core principle\.A chess variant in which royal status can be secretly transferred between a player’s own pieces\. The objective is to capture the opponent’s*Regent*— their current royal piece — which may or may not be their Original King\.

Terminology\.*Regent*: the piece currently holding royal status; capturing the opponent’s Regent wins immediately\.*Original King*: the piece that started the game as king\.*Crown Shift*: the secret act of transferring royal status to another piece\.*King Mode*: the Original King is the Regent, and standard chess rules apply to it\.*Regent Mode*: a different piece is Regent and gains royal immunity\.

Setup\.Both players begin in King Mode with their Original King as Regent; standard chess setup and rules otherwise apply\.

Crown Shift\.Available to each player from the start of their 4th turn, and again 15 completed moves after each use, tracked independently per player\. Usable even while in check or checkmate\. On one’s own turn, without declaration, a player may secretly designate any of their own pieces — including the Original King, returning to King Mode — as the new Regent\. The shift does not consume the turn: a regular move must still follow\. If checkmated in King Mode with Crown Shift available, the player may shift before any other action; shifting to a non\-king piece nullifies the checkmate, while shifting to the king, or not shifting, ends the game in a loss\. A shift onto an attacked square risks immediate capture and loss — the crown may be placed anywhere, including under attack\.

Game modes\.*King Mode*: standard chess rules and check restrictions apply to the Original King; castling is permitted, and possible, only here\.*Regent Mode*: the Regent moves by its own piece type’s rules, is immune to check restrictions, and its capture ends the game immediately; the demoted Original King retains one\-square movement, may sit on or move into attacked squares, cannot castle, and its capture is ordinary material loss only\.

Win conditions\.Capturing the opponent’s Regent wins immediately\. In King Mode, checkmate on the Original King with no Crown Shift escape is a loss\. In Regent Mode, traditional checkmate cannot occur, because the Regent is immune to check\.

Other rules\.A promoted Regent pawn automatically transfers royal status to the promoted piece\. Check is always announced against the Original King regardless of mode, and a Regent\-Mode player may legally ignore it\. Traditional stalemate is abolished: a player with no legal move passes automatically, with a draw only if both players pass on consecutive turns\. A pass does not count toward the Crown\-Shift cooldown or the 50\-move no\-progress rule, but does count toward the 75\-move backstop\. Draws also follow from the 50\-move rule \(reset by capture or shift\); the 75\-move backstop \(not reset by shift, counted in total plies, to prevent indefinite stalling\); threefold repetition on visible board state only, so a hidden Crown Shift between occurrences does not prevent the draw; and the bare\-kings dead position, all other material configurations remaining live because even a lone knight can win by capturing the Regent\. Castling requires King Mode, the Original King and a non\-Regent rook\. All other standard chess rules, including en passant, remain in effect\.

### A\.2Depth\-sensitivity and support diagnostics

Depth cutoffs\.The canonical cutoff is board ply≥8\\geq 8\. Two stricter prespecified cutoffs are reported for every condition on both endpoints\. No cutoff revises any condition’s canonical classification, which is the frozen basis for every main\-text claim\. Classifications are shown only where the design confers them: cells A–C prospectively, cell D descriptively, and E/F not at all\.

†Descriptive only: cell D ran in the immediately preceding serving window and completed before the A/B/C interleaved window opened, so its outcome preceded the rule freeze\.‡Exploratory; no classification is conferred\.§Outside the factorial and its classification scheme; the transport’s frozen protocol reports R2 at the canonical cutoff only\.

Two readings this table adds to the summary in Section[8](https://arxiv.org/html/2609.22478#S8): cells E and F show the identical descriptive pattern with no classification conferred, and F’s is the only R2 interval that spans zero at a stricter cutoff\. As in the main text, this is a descriptive re\-analysis, not a preregistered interaction test\.

Support diagnostics\.Both endpoints are support\-dependent \(Section[2](https://arxiv.org/html/2609.22478#S2)\), so the table below is required to read their magnitudes\. Support and residual statistics are reported over the R2\-scoreable population of each condition\. For the cross\-family transport the two available populations differ and are therefore named separately: mean named\-candidate support is8\.32468\.3246over its eligible belief plies \(n=1,186n=1\{,\}186, the value cited in the main text\) and8\.26918\.2691over its R2\-scoreable subset \(n=1,167n=1\{,\}167\); the true state falls in the unnamed residual on1\.77%1\.77\\%of eligible belief plies and1\.80%1\.80\\%of R2\-scoreable plies, and mean residual mass is0\.004470\.00447\. Neither pair may be reported without its population\.

In the median\-kkcolumn, — denotes a statistic not reported in the frozen artifact; no post\-hoc value was recomputed\. Every other cell in this table is a reported value, and no zero is represented by a dash\.

Capture\-time diagnostics\.A separate population again: one event per named candidate at capture\-time plies, scored as the ratio of model to matched\-uniform Brier loss, with high\-confidence commitments counted on the captured square\.

The cross\-family transport is deliberately absent from this table\. Its frozen protocol defines its capture diagnostics over captures of the*true Regent square*rather than over any capture, giving a proper\-score ratio of1\.6351\.635on6767such captures; that quantity and the column above are different populations and must not be placed on one axis\.

### A\.3Objective state\-richness stratification

Detail supporting Section[8](https://arxiv.org/html/2609.22478#S8)\. This analysis is exploratory relative to the frozen factorial design and was specified in full before any stratified value was computed\.

Definition\.KKis the number of live opponent pieces at the scored ply, read from public game state immediately before that ply’s move\. It is not a new quantity:KKis already the denominator of the frozen matched\-uniform comparator, so every eligible R1 event carries it\. Under the environment’s rules a Crown Shift may move royal status to any live own piece with no piece\-type restriction, so the set of squares that could hold the opponent’s Regent is exactly the set of live opponent pieces\. No hidden or model\-reported information entersKK\.

Focal stratum and support rule\.The focal stratum isK≥8K\\geq 8— at least half of an opponent’s starting pieces still live — which covers over 80% of eligible events in each core cell\. Support is judged by the study’s existing convention: fewer than 100 contributing game clusters isinstrument\-limitedand reported descriptively rather than inferentially\.

Cells E and F fall below the 100\-cluster floor and are descriptive only; no interval is presented for them and they form no part of the inferential high\-KKclaim\.

Cross\-identifier contrasts \(earlier minus later tested identifier\), under R\.AtK≥8K\\geq 8:\+0\.0277\+0\.0277, 95% CI\[\+0\.0128,\+0\.0414\]\[\+0\.0128,\+0\.0414\]at 4K \(A versus C\) and\+0\.0310\+0\.0310,\[\+0\.0172,\+0\.0446\]\[\+0\.0172,\+0\.0446\]at 16K \(B versus D\)\. The corresponding all\-KKcontrasts are\+0\.0373\+0\.0373,\[\+0\.0233,\+0\.0498\]\[\+0\.0233,\+0\.0498\]and\+0\.0367\+0\.0367,\[\+0\.0236,\+0\.0492\]\[\+0\.0236,\+0\.0492\]\. These contrasts are themselves new relative to the frozen design, which specified no cross\-cell test, and are exploratory on the same terms as the stratification\. The B\-versus\-D pairing additionally crosses serving windows\.

Attenuation, and what it is not\.The high\-KKcontrasts are modestly smaller than the all\-KKcontrasts — approximately 26% at 4K and 16% at 16K\. Two qualifications apply and neither is optional\. The intervals overlap substantially, and*no predeclared test establishes the attenuation itself*; it is a difference between two exploratory estimates, not a tested effect\. The direction is the one the existing depth signature already predicts, which is a consistency observation rather than independent evidence\.

Classification\.K1: the reversal persists clearly atK≥8K\\geq 8with support above the floor and intervals excluding zero, so late\-game candidate\-set collapse cannot by itself explain it\. The claim applies inferentially to the Gemini 3\.1 and 3\.7 cells only, and does not establish that state richness has no effect\.

Descriptive pattern, below the support floor\.Across the low \(K≤4K\\leq 4\), mid \(5≤K≤75\\leq K\\leq 7\) and high strata, the Gemini 3\.7 cells are comparatively flat while more of theKK\-dependence appears in the Gemini 3\.1 cells, whose low and mid strata are their worst\. Those strata fall below the support floor, so this is context rather than a claim — and it runs opposite to the direction a simple depletion account requires\.

Independent verification\.KKwas verified by a second derivation rather than restated: the canonical path replays recorded moves and Crown Shifts on the engine and counts live pieces, while the independent path counts pieces in each ply record’s own stored board state\. Every cell’s fullKKdistribution matched exactly, as did every event and cluster count, across 148 compared quantities, with no discrepancies beyond floating\-point summation order\.

### A\.4Well\-formedness and format integrity

Definitions\.A belief response is*well\-formed*if it parses to a valid candidate distribution obeying the frozen mass\-validity tolerance, which admits a total stated mass within0\.020\.02of11;*incoherent*if it is parseable JSON that violates a candidate\-set or mass\-tolerance constraint; and*malformed*if no valid JSON is recoverable at all\. Truncation — a call reaching the generated\-token ceiling — is recorded on a separate axis, because a truncated call can still parse as well\-formed if a complete object was emitted before the cutoff\. Responses that are not well\-formed are excluded from scoring rather than repaired\.

Denominator\.The population is the condition’s logged decision plies, as defined by the frozen scorer’s own integrity report: one record per model decision ply, partitioned by that record’s elicitation category\. This is the definitional denominator and is the one used below\. A numerically identical count is obtainable from the opportunity module, which replays the recorded move list and emits one entry per model\-mover ply; the two agree in every condition because the harness emits exactly one record per model decision ply, but only the former defines the quantity\.

Gemini 3\.7’s well\-formed rate is materially higher than Gemini 3\.1’s — roughly nine points, C/D against A/B — after normalising by decision\-ply count, so it reflects a lower failure rate and not merely a larger ply population\. Cell D’s 63 non\-well\-formed beliefs were verified individually: 62 are incoherent, a candidate\-set or mass\-tolerance violation on an otherwise\-parseable payload, and exactly one is malformed, with no valid JSON recoverable despite a normal, non\-truncated completion\. Stated with that exception: across all four core cells, every belief failure but that single case was a semantic failure on an otherwise\-parseable payload, and no belief response was truncated in cells A–D\. Cell E is the one condition anywhere in this study where the generated\-token ceiling materially bound generation, and its well\-formed rate nonetheless remains high for the reason given above\. Move calls were 100% well\-formed in every condition\.

### A\.5Same\-window measurement\-configuration control

Purpose\.The historical runs and their reconstruction differ in serving period and in measurement configuration at once, so neither source is identified by their difference alone\. This control holds the model identifier, ceiling, opponent, horizon, seed schedule and scorer fixed and varies the configuration bundle, within one day\.

Held constant\.The same public model identifier; the same serving window; a 4,096\-token generated\-output ceiling; the same fixed Tier\-1 opponent; a 150\-ply game horizon; one shared environment\-seed schedule; balanced 50/50 colour assignment; and the common R1 scorer\. One hundred games per arm\.

Configurations\.H is the historical harness and R the rebuilt native\-API instrument used for cells A–F\. They differ as a six\-component bundle, and the control does not resolve them individually\.

The rules\-document component\.This component could be mistaken for a change in the game, so it is stated exactly\. The two revisions differ by a single hunk at the end of the file — the document version block — and the difference contains no normative text\. Gameplay rules were therefore identical across the arms\. The reconstruction reads the archived revision, verified by recomputing the document digest at read time, and a counterfactual substitution of the current revision was run to confirm the check is capable of failing\. The rules text is read in a mode that normalises line endings, so platform line\-ending policy cannot perturb the digests\.

Both arms ran 100 games\. The serving\-period contrast is H\-current minus the historical 60\-game arm\. The H−\-R configuration contrast is primary: within the same\-day back\-to\-back comparison it measures the H\-minus\-R endpoint difference, while residual intra\-window serving variation cannot be excluded\. The serving\-period contrast compares one configuration across serving windows and is secondary by design, because the historical arm is fixed at 60 games: its interval half\-width cannot fall below0\.02540\.0254however much new data is collected, and the realised half\-width is0\.03200\.0320\. Its inconclusiveness is therefore a statement about precision, not evidence of equivalence\. The 20\-game historical arm \(\+0\.0593\+0\.0593,\[\+0\.0292,\+0\.0931\]\[\+0\.0292,\+0\.0931\]\) is reported only as descriptive sensitivity and is never pooled with the 60\-game arm\.

Integrity\.Both arms completed 100 of 100 games on the frozen seed schedule, with no errored games, no game reaching the 150\-ply horizon, and no truncated generations; every configuration field was single\-valued within each arm\. An independent reimplementation sharing no scoring code reconciled every compared quantity, with differences confined to floating\-point summation order\.

Format\-level behaviour\.Well\-formed elicitation rates were not identical across serving windows even under H: 82\.3% in the archived historical arm against 72\.1% \(1,212 of 1,682\) for H\-current, a difference of−10\.3\-10\.3percentage points, inside the prospectively frozen±15\\pm 15\-point diagnostic band\. This records that format\-level behaviour differed across windows under one configuration\. It is not evidence of a mechanism, and not evidence of a backend change\.

### A\.6Provenance milestones

Because this paper argues that a nominal model identifier is insufficient provenance, the execution record is made auditable here\.

Execution and freeze order\.Historical runs→\\rightarrowcell D, which motivated the grid→\\rightarrowcells A/B/C, frozen and sealed before any of their scientific outcomes were known and executed on interleaved schedules within one serving window→\\rightarrowthe Gemini 3\.8 extension design freeze→\\rightarrowcell E→\\rightarrowa sample\-size and status amendment→\\rightarrowcell F→\\rightarrowthe cross\-family transport, prospectively frozen and executed after the Gemini conditions concluded\. Cell D ran in the immediately preceding serving window and completed before the A/B/C interleaved window opened\.

The extension amendment\.The extension was initially frozen at 150 games per cell, before any call to the new identifier\. After cell E’s first 75\-game block completed, only prespecified operational information — runtime, cost, transport behaviour and output\-ceiling pressure — was inspected; no scientific endpoint, belief content or correctness signal from either cell was inspected or scored\. On that operational basis alone, and before cell F began, the design was amended to 75 games per cell and downgraded to exploratory\. Cell E therefore ran 75 games under the original confirmatory plan and cell F entirely under the amended exploratory one\.

Transport configuration\.The cross\-family transport was accessed through the OpenAI Chat Completions API at reasoning effort*high*and the provider\-default temperature of 1\.0, with a 16,384\-token generated\-output ceiling, the same fixed Tier\-1 opponent and split move/belief elicitation architecture as the core grid, and the same canonical 75 environment seeds already used for cell F\. Its sample size was fixed prospectively rather than by an outcome\-dependent stopping rule\.

The identifier interval\.The historical and reconstructed Gemini 3\.1 conditions share the identical public model identifier across an 18–21 day interval, the historical runs preceding the reconstructed ones\. This is the paper’s central provenance point, stated auditably\.

Metadata\-resolution audit asymmetry\.Only the Gemini 3\.8 identifier received an explicit provider model\-metadata resolution audit; the provider\-returned resolved version string was3\.0, carrying no preview or experimental marker\. No equivalent resolved\-version audit exists forgemini\-3\.1\-flash\-liteorgemini\-3\.7\-flashin any execution window, including the historical runs and their reconstruction\. This is an asymmetry in how firmly the served endpoint behind each identifier was verified\. It is not evidence that any identifier resolved to something unexpected: nothing here indicates the unaudited identifiers were wrong, only that our records cannot demonstrate what they resolved to\. It is a real provenance gap, and precisely the condition under which this paper’s snapshot\-immutability limitation applies\.

Anonymity\.Repository, commit and account identifiers, and internal execution timestamps, are omitted throughout\. The sequencing above is the scientifically load\-bearing content and is stated exactly\.

### A\.7Elicitation\-format feasibility studies

Detail supporting Section[3](https://arxiv.org/html/2609.22478#S3)\. Three protocols were tested before the factorial grid, each prospectively frozen with its own read order, classification rule and prohibited\-quantity list, all against the fixed Tier\-1 opponent with the evaluation design otherwise unchanged\. Belief elicitation is stateless, so both formats in a given comparison could be issued at the identical pre\-move state within one game, making each comparison paired\.

Blinding\.Each protocol’s frozen ruling was forbidden to inspect Regent truth, correctness, proper scores or acted\-on probability\. These studies therefore say nothing about what scientific belief\-quality result an exhaustive protocol would have produced; they speak only to whether it could be elicited at all, and how stably\.

Protocol B: self\-enumerated full support\.The model reconstructs the live candidate set and assigns a probability to every member, with no residual category\. Non\-inferiority marginM=−0\.15M=\-0\.15, fixed before execution\.

The ply 1–25 band is a required, well\-powered band with all 24 games contributing, and its entire interval lies below the margin:NO\-GO\. The two later bands areunresolvedat small sample sizes, on 3 and 2 contributing games respectively, so the formal decision rests on the prespecified 1–25 band alone and not on any pooled result\. Well\-formedness in that band fell from 90\.4% \(302 of 334\) under top\-kkplus residual to 24\.6% \(82 of 334\) under full support\.

*Failure taxonomy\.*Of 369 non\-well\-formed full\-support responses, 182 named a candidate that was not live and 172 omitted one that was, while only 15 violated the mass tolerance — and there were zero malformed responses in either arm\. So 354 of the 369 failures are failures to name the exact live candidate set\. What collapsed was the model’s ability to enumerate that set, not its ability to produce structured output\.

Protocol C: roster\-supplied positional elicitation\.The harness supplies the exact live\-candidate roster and the model returns a probability vector aligned to it\. Structural feasibility improved substantially relative to self\-enumeration\. A validation permuting only roster order, with board state, history and candidate set held fixed, then found that on every one of the 3 genuinely informative states, cross\-order variation exceeded same\-order replicate variation, by factors of2\.00×2\.00\\timesto15\.00×15\.00\\times\. The frozen closure language is retained rather than upgraded: the positional\-vector representation exhibited credible presentation\-order sensitivity beyond ordinary same\-condition stochastic variation on informative states, and is therefore not sufficiently stable for downstream belief\-quality analysis under this configuration; the roster\-supply insight is retained, the positional response encoding is not\.

Protocol D: identity\-anchored roster supply\.Each probability is bound explicitly to a named candidate rather than a vector position, removing transcription between position and identity as a failure mode\. Two distinct instrument properties were assessed\.

*D\-F1, structural feasibility*against concurrent top\-kk: meanDF​1=\+0\.2235D\_\{F1\}=\+0\.2235, 95% CI\[\+0\.0824,\+0\.3647\]\[\+0\.0824,\+0\.3647\], against the sameM=−0\.15M=\-0\.15margin — entirely above it, a formalGO\. One supporting statistic is retained: Protocol\-D well\-formedness on the canonical call was 71 of 85\.

*D\-F2, presentation stability*: mean total\-variation distance between responses to states differing only in hypothesis presentation order,0\.18090\.1809, 95% CI\[0\.1247,0\.2395\]\[0\.1247,0\.2395\], achieved half\-width0\.05740\.0574against a frozen precision target of0\.100\.10— the declared precision target was met\. Five qualifications travel with this estimate\. \(i\) D\-F2 was an*estimation study with no prespecified pass or fail threshold*; its interval lying above zero is evidence about the size of a presentation effect, not a verdict against a criterion\. It is therefore*not*a failed test, and no threshold is supplied after the fact in order to make it one\. \(ii\) It was computable on 49 of 85 formal states, 57\.6%, because it required four independently well\-formed responses per state; the complementary 36 states were unscoreable\. \(iii\) The estimate is conditional on that all\-four\-well\-formed subset and should not be assumed to characterise the full formal\-state population\. \(iv\) No direction of that selection effect is identified:0\.18090\.1809is*not*a lower bound or a floor, and no separate analysis establishes that the unscoreable states would have shown greater instability\. \(v\) It does not reverse D\-F1, which tests a different instrument property — the structural feasibility of one canonical call, versus the stability of the full response under an irrelevant change of presentation\. A single call can be reliably well\-formed while repeated exhaustive elicitation at the same state remains brittle\. Signs across the 49 scoreable states were 35 positive, 9 zero and 5 negative\.

Scope rule\.Development stopped at Protocol D under the prospectively frozen scope rule; no fourth protocol was designed\. On review, the residual presentation sensitivity was judged too large to treat identity\-anchored full support as sufficiently stable to carry downstream belief\-quality analysis under the tested configuration\. The protocols characterise one model and one configuration; a different model might enumerate reliably\.

### A\.8Within\-choice belief\-action alignment ancillary

Before the factorial grid was designed, a descriptive analysis on the historical corpus asked whether the captured square received more stated probability than explicitly named, unchosen, capturable alternatives on the same ply\. Eligibility required both the selected target and at least one capturable alternative to be explicitly named, which only 32 plies across 23 games satisfied\. Within that subset, the captured square received on average\+0\.2184\+0\.2184more stated probability than the mean named unchosen alternative\.

Two restrictions bound the reading\. The subset is unrepresentative of capture behaviour by construction: 73\.6% of historical captures targeted a square never named at all, and those plies cannot enter the comparison\. And requiring alternatives to be named fixes the choice set, which makes the comparison well\-defined but does not establish why the model chose as it did — a model may capture a piece for material reasons while also having assigned it more Regent probability than the other capturable alternative\. The defensible reading is only that, among explicitly represented capturable alternatives, the chosen target tended to receive higher stated Regent probability than the unchosen ones\. It is not a claim about why the choice was made, and not a calibration claim\. The opportunity\-conditioned analysis of Appendix[A\.11](https://arxiv.org/html/2609.22478#A1.SS11)supersedes this measure conceptually, by conditioning on a population where belief is unambiguously actionable and the relevant action is unambiguously relevant; this measure is retained because it is the historical one and its restriction is instructive\.

### A\.9Public\-information reference tracker

Historical and auxiliary context\. This material is not part of the factorial result reported in Section[6](https://arxiv.org/html/2609.22478#S6), and nothing in the main text depends on it\.

Mechanics\.A predecessor study built a hand\-specified belief tracker that replays a recorded game and maintains a distribution over which opponent piece holds royal status, updated only by deductively valid rules keyed to observable game events: a check response on the Original King; elimination of a captured piece when the game did not end; castling; and the pre\-shift timing window within which royal status cannot yet have moved\. The tracker never receives the opponent’s true Regent identity; ground truth enters only as the label against which its predictions are scored\. One implementation detail is worth stating plainly: the capture rule is gated on a stored field recording whether a capture ended the game, so the code reads a ground\-truth value — but what that field stands for, namely that the game ended, is publicly observable, and no hidden\-state information is gained from it\. Where this tracker is described elsewhere as certificate\-based, that refers to the logical validity of the individual rules, not to an exhaustive predictor\.

Results\.Scored against the matched\-uniform comparator on the historical capture\-only population at board ply≥8\\geq 8, by paired bootstrap on the identical events:

The original batch shows a small advantage whose interval excludes zero marginally; the replication, which is the better\-powered of the two, shows an interval that spans zero\. Against an underlying Brier scale of roughly0\.0170\.017–0\.0240\.024both point estimates are tiny, on the order of one to three percent in relative terms, and they are reported as such rather than as a robust demonstration in either direction\.

A withdrawn interpretation\.An earlier interpretation treated this tracker as an existence proof that the hidden state is predictable at these moments\.*That interpretation was withdrawn*, and the reason is specific: later inspection found that the per\-ply certificate overlay was not current at any of the scored capture queries, so the realised tracker had considerably less power than the phrase “exact tracker” would suggest, and its high\-confidence predictions arose from structural elimination alone\. The strongest defensible reading is narrow: on this opponent and this population, a public\-information tracker of this design obtains very little predictive advantage\. It is used in Section[8](https://arxiv.org/html/2609.22478#S8)only as limited\-headroom context, and not as a stronger comparator, not as a tractability certificate, and not as evidence of post\-shift predictability\.

Engine\-defect insulation\.A later engine audit found a stale post\-terminal Regent pointer after the winning move was pushed\. This result is unaffected, and the reason rather than the assertion is what matters: the tracker records the true Regent label*before*the terminal move is pushed, and does not consume the affected field\.

Predictability and calibration are different questions\.Where public evidence is weak, appropriate uncertainty is itself the calibrated response, so low raw predictability does not make confidence\-versus\-outcome scoring meaningless\. The opponent’s shift timing is additionally only partly state\-responsive by policy \(Section[4](https://arxiv.org/html/2609.22478#S4)\), which bounds what any public\-information predictor could achieve on this population\.

### A\.10Numerical audit note

Every reported number in this manuscript was checked against its source scoring artifact\. Most are stored fields checked by direct read: R1 and R2 deltas and intervals at all three depth cutoffs for A–D, E/F and the transport; the candidate\-support and capture diagnostics; the opportunity\-analysis tables; and the historical comparison table\. A systematic audit checked every A–F R1/R2 estimate and interval bound, at all three reported cutoffs, against the frozen artifacts, and the manuscript and its figure sources report the canonical artifact values throughout\.

One pair required reconstruction rather than a direct field read\. Cell D’s absolute R2 Brier values — model0\.73750\.7375and matched uniform0\.84030\.8403, quoted in Section[8](https://arxiv.org/html/2609.22478#S8)— are not themselves returned by the frozen R2 scoring function, which reports only the difference\. They were recovered by re\-running the frozen per\-ply R2 formula over the D corpus and separately averaging the model and uniform components before differencing: recovered model0\.73751555374945740\.7375155537494574and uniform0\.8402994072464350\.840299407246435onn=2,307n=2\{,\}307scoreable plies, matching the reported figures and reproducing the already\-frozen delta of−0\.102784\-0\.102784exactly\.

One presentational point is recorded for completeness\. The historical 20\-game arm’s endpoint is\+0\.0593\+0\.0593at four decimal places, the direct rounding of its stored value, and that form is used at every occurrence in this paper\.

### A\.11Opportunity\-conditioned analysis: full cross\-tabulations

Definition\.An opportunity exists on a ply, for the model’s own turn, if and only if the opponent is in Regent Mode, the true Regent square is known to the engine, and at least one legal move captures it\. The analysis is only possible while the opponent is in Regent Mode, so the pre\-shift window contributes zero opportunities by construction\.*Converted*means the chosen move is exactly such a capture\. This analysis is ancillary and descriptive throughout: it introduces no inferential test and does not modify R1 or R2\.

The historical within\-choice analysis of Appendix[A\.8](https://arxiv.org/html/2609.22478#A1.SS8)asks a related question on a differently constructed population: it is restricted to plies where the eventual capture target was itself among the model’s named candidates, whereas the analysis here conditions on positions in which belief is unambiguously actionable, whether or not the true state was named\.

Provenance differs by condition, and the difference is material to how each row reads\. The historical corpus and cells A–D were scored post\-hoc, under a specification written after those results already existed\. The E/F specification was frozen before scientific unseal — outcome\-blind at freeze, though not prospective in the strong sense the core grid’s endpoints were\. The transport’s opportunity analysis was prospectively frozen before execution\.

All values below are from the corrected implementation described under*En\-passant semantic correction*\.

Named, top\-ranked andp≥0\.5p\\geq 0\.5rates are over the usable\-belief population; conversion is over opportunity plies; and conversion\-given\-p≥0\.5p\\geq 0\.5is over the smaller population that reached that threshold\. In the newer conditions the true Regent is represented on 97\.9–100% of usable\-belief opportunity plies, top\-ranked on 28\.1–34\.7% and assignedp≥0\.5p\\geq 0\.5on 16\.3–22\.4%; once that threshold is reached the available win is usually taken\. The co\-variation with tested identifier does not identify a causal mechanism\.

En\-passant semantic correction\.The frozen semantic definition of an actionable opportunity has always been that there exists a legal move capturing the true Regent\. A post\-unseal audit found that the canonical implementation approximated this as move\-destination\-square equality, which is correct for every ordinary capture and capturing promotion but misses en\-passant captures, whose destination differs from the captured piece’s own square\. Correcting the implementation changed the opportunity denominator by exactly one ply each in cells C, D and F \(334→335334\\rightarrow 335,346→347346\\rightarrow 347,195→196195\\rightarrow 196\) and the conversion numerator by one ply in cell C only \(147→148147\\rightarrow 148, an already\-converted capture newly recognised as an opportunity rather than newly converted\); cells A, B, E and the transport were unaffected\. The three affected plies were individually confirmed to change no rate in direction, since none was top\-ranked or stated atp≥0\.5p\\geq 0\.5under either filter\. Primary R1 and R2 endpoints were not recomputed and are unaffected, because the opportunity module is not part of their scoring path\. Regression tests cover the en\-passant case, an ordinary capture, a capturing promotion, and castling, which can never register as a capture under either filter\. The original result artifacts were retained unchanged, with the correction recorded separately, and every value in this subsection and in Figure[4](https://arxiv.org/html/2609.22478#S7.F4)is the corrected one\.

Post\-hoc gameplay and material\-depletion context\.Across the 825 games in the core grid, extension and transport combined, 822 ended by a Regent capture on either side and 3 by repetition draw, with zero games ending by checkmate after canonical classification\. Terminal Regent captures are late events: the median capture ordinal is the 13th–14th of the winning side’s captures, with a median of 3–4 opponent pieces remaining immediately before it, the about\-to\-be\-captured Regent included\. Winning trajectories nonetheless contain few genuine actionable opportunities — a median of 2–3 per winning game, with 1–2 missed before the terminal capture\. Read together, these are not the signature of many repeated chances being squandered until the board clears: most non\-Regent captures occur in phases where the true Regent is not yet an actionable target at all, and once an actionable opportunity exists it is usually taken quickly\. This is a post\-hoc descriptive characterisation, not a prespecified endpoint, and it does not establish robustness to opponent strength\.

Opponent\-regime engineering check\.After the primary experiments, engine\-only checks of stronger information\-symmetric opponent configurations were run, against frozen acceptance bands\. In a designated\-side medium\-versus\-medium reference replay, 60% of games contained at least one actionable true\-Regent opportunity; this fell to 8% against a Tier\-1 Hard configuration and to 3–4% against the tested Tier\-2 search configurations, despite at least 99\.5% of games reaching ply 14 and Crown Shifts occurring in all games\. Trajectory length and hidden\-state activity therefore do not guarantee adequate opportunity density\. These were post\-hoc engineering checks, not study endpoints, and no reported result depends on them\. No tested stronger configuration cleared both the strategic\-challenge and opportunity\-yield criteria; the intermediate design space remains largely unexplored, and no monotonic strength\-to\-opportunity relationship is claimed from three tested points\.

### A\.12Independent reimplementation

Every reported quantity in this study was checked by an independent reimplementation sharing no code with the canonical scoring pipeline, built from the frozen endpoint definitions and specification documents alone\.

For the prospective core cells every confidence interval reproduced under the same clustered bootstrap and seed\. The 162 quantities compared there are divided equally across cells A, B and C; the descriptively reported D cell was reproduced separately under its own audit and is not among them\. Of those 162, 135 agreed bit\-for\-bit and 27 agreed to within the10−610^\{\-6\}tolerance without being bit\-identical\. Those 27 are the R1 delta and both interval bounds at each of the three reported depth cutoffs in each of the three cells; they differ by at most1\.1×10−141\.1\\times 10^\{\-14\}, which is floating\-point summation\-order noise, and every R2 quantity and every classification field matched exactly\. No reported figure at its printed precision, no interval interpretation, no endpoint classification and no conclusion changes\. For the extension, an implementation that reconstructed all board mathematics from primitives differed only on R1 deltas and interval bounds, by10−1510^\{\-15\}to5×10−155\\times 10^\{\-15\}, which is floating\-point summation\-order noise; R2 matched exactly throughout\. The opportunity reimplementation reproduced all compared quantities exactly across all seven conditions, including the full high\-confidence case listings\. For the transport, a second implementation was built by a separate development pass from the frozen protocol prose alone, sharing no scoring code and independently replaying game legality rather than importing the canonical opportunity module; two implementation\-side bugs were found during reconciliation, both in diagnostic computation and never in the R1/R2 endpoints, which matched from their first comparison, and both were root\-caused and fixed before the result was finalised\. Independent replay verified board\-state alignment on sampled plies with zero mismatches throughout\.