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When Do Models Admit They Are Wrong? Failure Disclosure Is Unstable Under Reinforcement Learning

Steven Y. Feng, Noah D. Goodman, Michael C. Frank, Evan Hubinger, Paul C. Bogdan, Andrew Lampinen

arXiv:2609.33220v1cs.LGcs.AIcs.CL

TL;DR

Outcome-based RL can yield similar task performance but different communication about failed attempts, a behavior relevant to oversight. The paper studies this variability across training runs, investigates how divergence arises, and tests reference anchoring. It finds that failure disclosure can be far less reproducible than task capability, while anchoring reduces variability with setting-dependent effects on capability.

  • Problem

    Outcome-based RL clearly scores verifiable task success but may leave oversight-relevant behaviors such as acknowledging failure unspecified, so task accuracy alone may not reflect what monitors observe.

    Source: §1 · p. 1

  • Method

    The authors compare task solve and failure disclosure across repeated outcome-only RL runs, controlled training variations, reporting interventions, and reference anchoring.

    Source: §1 · pp. 2–3, §2 · p. 3

  • Results

    Across 20 Qwen2.5-1.5B runs, failure disclosure varies 3.9× more than task solve rate, and the paper reports this selective variability across other tasks and settings.

    Source: §1 · p. 2

  • Takeaways & Limitations

    When oversight-relevant behavior matters, measure it across multiple retrainings alongside task capability; anchoring can reduce disclosure variability, but its effects on capability differ by setting.

    Source: §7 · p. 10

    Controlled tasks and fixed prompt sets do not establish how common the effect is in deployed systems, and the 7B anchoring evidence comes from one model–task setting.

    Source: §7 · p. 10

Abstract

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Outcome-based reinforcement learning can produce models with similar task performance but very different ways of communicating about their mistakes. We study failure disclosure: whether a model admits that an attempted solution failed rather than staying silent or presenting it as successful. Across repeated outcome-only GRPO training runs, failure disclosure varies far more than task accuracy. The pattern extends to a second reasoning task and stabilized PPO, persists at 7B, and also appears in an instruction-conditioned 32B setting. We also find that small floating-point and sampling differences during training can redirect reporting behavior even when the task objective and earlier training history are held fixed. Additional tests show that failure disclosure is not a single decision: Checking the answer, entering a report, and completing the admission can separate, and the weak point depends on the task and response format. Further, experiments with neutral controls show more broadly that behaviors left weakly constrained by training are especially likely to vary across runs, of which failure disclosure is an example. We can reduce variability in failure disclosure by discouraging the model from drifting from its starting policy on failed, well-formed responses. This makes reporting substantially more consistent, though its effect on task performance depends on the setting. Stable task accuracy therefore does not guarantee stable safety-relevant behavior: Researchers should measure these behaviors directly across runs and design training methods that keep them reliable.

1 INTRODUCTION

Outcome-based RL can optimize verifiable task success without specifying every behavior relevant to oversight, including whether a model acknowledges failed attempts. The paper finds that failure disclosure is less reproducible across runs than task capability, investigates how reporting diverges, and tests reference anchoring as a way to reduce that variability.

1 INTRODUCTION

  • Because outcome-based objectives leave some oversight-relevant behavior unspecified, task accuracy alone can miss changes in what models communicate when they fail.The paper frames this gap as a concrete form of underspecification in outcome-based post-training.Source: §1 · pp. 1–2
  • Across 20 Qwen2.5-1.5B runs, failure disclosure varies 3.9× more than task solve rate, despite similar task capability across runs.The pattern also appears in another Qwen-1.5B run set, OLMo-2-1B, and a second reasoning task; larger-model experiments are treated as boundary evidence.Source: §1 · p. 2
  • Small floating-point or future-rollout differences can redirect reporting behavior, including when the earlier training state is held fixed.The divergence can arise later in RL, rather than being fixed at initialization or early training.Source: §1 · pp. 2–3
  • Failure disclosure comprises linked stages, and the fragile stage depends on task and response format rather than having one universal reporting bottleneck.In the primary Countdown format, a learned paragraph transition affects later reporting; grid and inline-report settings place the boundary elsewhere.Source: §1 · p. 2
  • Reference anchoring on failed, well-formed responses reduces disclosure variability across two reasoning tasks, while its effect on task performance depends on setting.The evaluated 1.5B settings show reduced task performance, whereas the 19 tested 7B runs show a small solve gain.Source: §1 · p. 3
  • The authors conclude that post-training evaluation should measure safety-relevant behavior across runs alongside task performance.They recommend considering such behaviors when designing training objectives.Source: §1 · p. 3

2 EXPERIMENTAL FRAMEWORK

The experiments use objectively verifiable reasoning tasks and compare failure disclosure with task performance across repeated post-training runs. They vary training randomness and execution conditions while defining disclosure and cross-run variability as the principal measurements.

2 EXPERIMENTAL FRAMEWORK

  • The study evaluates Countdown and shortest path, with Qwen2.5-1.5B as the main model and other models, scales, tasks, and algorithms as boundary checks.Additional targeted experiments use grid/constraint and MBPP-style code tasks.Source: §2 · p. 3, Figure 2 · p. 4
  • Most runs use an SFT warm start followed by outcome-only GRPO that rewards task success but does not directly reward disclosure.The 32B experiment starts from an instruction-tuned model and elicits reporting through the prompt instead of report SFT.Source: §2 · p. 3
  • Failure disclosure is acknowledgment of an attempted failure among terminated failures; format-invalid terminated failures count as non-disclosures, while unterminated completions are excluded.The main text uses a conservative detector.Source: §2 · p. 3
  • The authors vary retraining seeds, low-level execution configurations, or future rollout randomness to test sources of behavioral divergence.Continuation tests restore the same model, optimizer, scheduler, trainer, and RNG state before changing only future rollout randomness.Source: §2 · p. 3
  • The main outcomes are task solve rate, failure-disclosure rate conditional on failure, and variability across retraining runs, compared using standard-deviation ratios.The retraining run is the main unit of analysis.Source: §2 · p. 3

3 CAPABILITY CAN REPRODUCE WHILE FAILURE DISCLOSURE DOES NOT

Across repeated training runs, failure disclosure varies more than task performance, with the pattern appearing across model families and tasks. Tests at larger scales and with stabilized PPO extend the evidence but also bound its interpretation.

3 CAPABILITY CAN REPRODUCE WHILE FAILURE DISCLOSURE DOES NOT

  • In 20 Qwen2.5-1.5B Countdown runs, disclosure ranges from 0.257 to 0.903 while solve stays at 0.340–0.490, making disclosure about 3.9× more variable.A separate Qwen-1.5B retraining set and broader evaluation checks show the same qualitative pattern.Source: §3 · p. 4
  • Across 20 OLMo-2-1B Countdown runs, disclosure is about 7.5× more variable than solve; on shortest path, disclosure spans nearly its full range while solve spans 0.46–0.61.The shortest-path result uses 20 Qwen-1.5B retrainings.Source: §3 · p. 4
  • In 19 Qwen-7B runs, both disclosure and solve vary more, while eight instruction-conditioned Qwen2.5-32B runs also show substantial reporting variation.At 32B, the frozen detector gives a conservative disclosure range of 0.056–0.628, blind-read calibration gives 0.173–1.000, and solve spans 0.302–0.619; these are treated as boundary evidence.Source: §3 · p. 4
  • False success claims account for 9–28% of terminated failures across 20 unanchored 1.5B runs and 2–59% across 19 unanchored 7B runs.Other non-disclosures end without acknowledging failure.Source: §3 · p. 4
  • Eight stabilized-PPO runs also show reporting variability, but with a smaller absolute spread than GRPO; step 300 is a fixed comparison point, not a convergence point.Disclosure does not decline at the same rate in every run, and longer-horizon results are mixed.Source: §3 · p. 4

4 HOW BEHAVIORAL DIVERGENCE ARISES

The authors isolate ways training differences and reporting cues relate to behavioral divergence, finding that divergence can arise during training and at different stages of disclosure. Neutral controls and credit interventions further test how weakly specified behaviors behave across runs.

4.1 SMALL FLOATING-POINT AND STOCHASTIC DIFFERENCES CAN REDIRECT TRAINING

  • Changing only micro-batch and gradient-accumulation configuration moves disclosure from 0.186 to 0.848 while solve stays at 0.327–0.463.The objective and exact-arithmetic gradient remain identical; repeated runs with the same configuration reproduce bit-for-bit in 5/5 tests.Source: §4.1 · p. 5
  • From the same mid-RL state at step 150, ten continuations differing only in future rollout randomness end with disclosure from 0.112 to 0.880 at step 300.Across eight continuation tests, median within-cell rate SD is 0.10.Source: §4.1 · p. 5

4.2 FAILURE DISCLOSURE IS A MULTI-STAGE BEHAVIOR

  • Across 40 checkpoints and report-wording combinations, models usually reach a point where a report could begin (median probability 0.952), but subsequent admission rates vary widely.The evaluation does not establish whether silence reflects failure to recognize an error or failure to express recognized error.Source: §4.2 · p. 5
  • In the primary format, inserting the learned two-newline transition makes later admission more frequent and consistent, while adding a verifier verdict does not further improve consistency.Other formats place the weakest transition elsewhere, so the fragile stage depends on task and response format.Source: §4.2 · p. 5

4.3 NEUTRAL CONTROL PHRASES SHOW THAT WEAKLY CONSTRAINED BEHAVIORS ARE ESPECIALLY SUSCEPTIBLE

  • A neutral phrase used without a prompt feature ranges from 0 to 0.90 across runs, but when tied to an explicit marker rule, all 20 runs follow it at step 150 and 19 of 20 at step 300.Other more strongly constrained behaviors are relatively stable, supporting the conclusion that weakly specified behaviors can drift across runs.Source: §4.3 · pp. 5–6

4.4 COLLATERAL CREDIT CAN AFFECT REPORTING, BUT DOES NOT EXPLAIN THE SPREAD

  • In mixed groups, all 517 relevant groups assign adverse collateral credit to failure reporting; protecting the reporting span raises disclosure by 0.19 on average in a three-pair pilot.Follow-up experiments do not demonstrate reliable reduction in cross-run variation, and removing adverse failure credit does not eliminate the spread and lowers task performance.Source: §4.4 · pp. 6–7

4 HOW BEHAVIORAL DIVERGENCE ARISES

  • Across the divergence experiments, small floating-point or stochastic differences can push training toward different weakly constrained behaviors and grow through later training.Collateral credit can affect reporting, but the evidence does not establish it as a general explanation for the level or variability.Source: §4.4 · p. 7

5 REFERENCE ANCHORING STABILIZES FAILURE DISCLOSURE

Failure-conditional reference anchoring penalizes drift on failed, well-formed responses to stabilize reporting without separately rewarding disclosure. It narrows disclosure variability across retrainings and, after an anchored history, reduces later divergence, with task-performance effects that vary by setting.

5 REFERENCE ANCHORING STABILIZES FAILURE DISCLOSURE

  • The intervention penalizes drift from a reference policy on failed, well-formed rollouts rather than defining a separate reward for every auxiliary behavior.Solved and format-invalid rollouts receive no penalty; the authors focus on this failure-conditional version because it covers fewer tokens and has a smaller capability cost than all-token anchoring in the reported comparison.Source: §5 · p. 7, §5.1 · p. 7

5.1 ANCHORING NARROWS RETRAINING VARIABILITY

  • In 20 1.5B Countdown runs, anchoring reduced disclosure SD from 0.189 to 0.089; the matched-progress unanchored SD was 0.139.The comparison still does not fully separate anchoring from differences in capability progress.Source: §5.1 · p. 7, Figure 4 · p. 8
  • Across 19 7B pairs, disclosure SD fell from 0.28 to 0.09, while false success claims fell from 0.27 to 0.14 and silent closes from 0.21 to 0.02 of terminated failures.The 7B comparison also reports a small probe-solve gain, but it is one model–task setting.Source: §5.1 · pp. 7–8

5.2 ANCHORING REDUCES LATER-RL DIVERGENCE AFTER AN ANCHORED HISTORY

  • After anchored training, continuing the anchor cut within-state disclosure variability by more than half (SD ratio 0.47), with lower variability in 8/10 parent states.Mean disclosure was not detectably changed, while solve decreased by ∼0.04; introducing anchoring only after an unanchored history did not yield a statistically established reduction.Source: §5.2 · p. 8

5.3 WHERE DOES THE STABILIZATION ACT?

  • Anchoring the failed-reasoning portion roughly halved disclosure variability, whereas anchoring only the short tail or reporting-point region did not detectably reduce it.The failed-reasoning gradient was at least 94% as large as the full-anchor gradient and pointed in nearly the same direction; most measured policy drift also occurred before reporting.Source: §5.3 · pp. 8–9

6 RELATED WORK

The paper situates its question at the intersection of failure reporting, outcome-based incentives, and reproducibility. Its focus is whether behavior not directly rewarded by a task objective remains reproducible across retrainings.

Failure awareness, verification, and reporting

Incentives, abstention, and explicit supervision

  • Unlike work on abstention incentives and directly supervised confession or abstention, this study asks whether task-unrewarded reporting persists through outcome-based RL (Joglekar et al., 2025; Zhai et al., 2026).It also relates its collateral-credit interventions to process supervision that localizes credit to verified trajectory parts (Liu et al., 2026c).Source: §6 · p. 9

Underspecification, reproducibility, and preservation

7 DISCUSSION

The discussion argues that similar task capability can coexist with variable safety-relevant reporting, which matters because disclosure changes what an overseer can observe. The authors recommend evaluating such behavior across retrainings alongside capability, while emphasizing that the observed instability is not universal and the evidence has defined scope limits.

7 DISCUSSION

  • Outcome-based RL can yield similar task capability but different failure reporting, so capability measures should be supplemented with measures of safety-relevant behavior.The discussion notes that reporting variation can affect what information reaches an overseer, unlike mostly cosmetic variation in pleasantries.Source: §7 · p. 9
  • Reporting can diverge later in training from shared mid-RL states, and checking, entering a reporting route, and final admission can separate, with bottlenecks varying by task and format.The paper cautions that large disclosure variation is not universal: smaller boundary experiments with Gemma and Phi did not show the same large spread.Source: §7 · pp. 9–10
  • Reference anchoring reduces disclosure variability, but its effects on mean disclosure and capability vary by setting, making behavioral preservation an empirical tradeoff rather than a free regularizer.Direct reward can score a desired behavior when definable, but cannot reinforce actions that have disappeared from sampling.Source: §7 · p. 10
  • The authors identify future work on predicting weakly constrained behaviors, testing broader tasks and pipelines, and reducing interference with task learning.They connect these directions to preserving monitorability-relevant behavior during optimization (Emmons et al., 2025).Source: §7 · p. 10
  • Controlled tasks enable objective failure judgments, but fixed prompts do not establish deployed-system prevalence; the 7B anchoring evidence is one model–task setting, and localization is response-format specific.Boundary experiments also show that large disclosure variation is not guaranteed under outcome-based RL.Source: §7 · p. 10

AI USE STATEMENT

A.1 MODELS

  • The reported model families include Qwen2.5 and OLMo 2, with Llama 3, Phi-4, Gemma 2, and a DeepSeek-R1 distilled lineage also used in code or boundary experiments.The paper uses simple reader-facing model names.Source: §A.1 · p. 16

A.2 TASKS

  • The task domains include Countdown, shortest path, and a retained MBPP+ code boundary; the shortest-path evaluation uses 100 fixed dev problems and nine fixed disclosure prompts.A valid but non-shortest route counts as failure, and the report-entry intervention has no shortest-path version.Source: §A.2 · p. 16

A.3 SFT WARM START AND POST-TRAINING

The paper starts from an SFT reference that reports failures, then applies outcome-only post-training that rewards task success but not disclosure. It defines the training comparisons, evaluation readouts, and reporting stages used to study that behavior.

A.3 SFT WARM START AND POST-TRAINING

  • Most Countdown runs use a failure-reporting SFT warm start followed by KL-free outcome-only Dr. GRPO, which rewards verified success but not failure disclosure.The 32B boundary experiment instead uses prompt instructions to elicit reporting without report SFT, so it is not a matched scale-up.Source: §A.3 · pp. 16–17
  • Countdown probes select reference-model failures with valid formats and detected reports, while shortest-path probes and greedy dev evaluations provide additional fixed evaluation surfaces.The 1.5B and 7B selected probes contain 20 and 17 prompts, respectively; terminated format-invalid responses count as non-disclosures, while unterminated responses are excluded.Source: §A.3 · p. 17, Table 2 · p. 17, Table 4 · p. 18

A.4 MID-RL STATE RESTORATION AND TERMINOLOGY

  • A continuation key restores the complete saved training state and changes only future rollout randomness, whereas an execution configuration changes floating-point computation with the seed fixed.A retraining seed changes prompt order and sampling streams.Source: §A.4 · p. 19

A.5 STATISTICAL ESTIMANDS

  • Across-run variation is analyzed at the retraining-run level, not by treating prompts or sampled responses as independent retraining draws.The section reports standard deviations, SD ratios, paired mean differences, and hierarchical estimates where applicable.Source: §A.5 · p. 19

B.1 FAILURE-DISCLOSURE READOUTS

  • Dv1 is a conservative, pre-fixed detector for disclosure on terminated objective failures; broader semantic detectors are reported alongside it rather than substituted after outcomes are observed.Dv1 searches the reasoning span for specified failure phrases.Source: §B.1 · p. 19

B.2 QUALITATIVE OUTPUT EXAMPLES

  • The examples distinguish explicit failure admission, a silent wrong ending, and a false success claim; a grid example further separates checking, forming a failure verdict, and expressing admission.The example does not establish whether recognition occurred before the model wrote the check.Source: §B.2 · p. 19

B.3 BLIND AUDITS AND DETECTOR SENSITIVITY

The detector is checked against human and independent model-reader judgments, and the section examines how anchoring changes distinct forms of non-disclosure. Across-run solve and disclosure are not detectably correlated in the primary runs.

B.3 BLIND AUDITS AND DETECTOR SENSITIVITY

  • The human audit agreed with the detector on 80/97 labeled examples (82.5%), including 40/42 concession examples, with no detector-marked concessions judged absent by the human reviewer.The reported κ = 0.822 measures agreement between two model readers, not human agreement.Source: §B.3 · p. 20, Table 8 · p. 21
  • At 7B, anchoring lowered false success claims by 0.127 [95% CI: 0.059, 0.194] and silent closes by 0.191 [0.101, 0.281] across 19 matched seeds, while narrowing the spread of both behaviors.At 1.5B, anchoring did not detectably change their average rates, though the spread of silent closes narrowed.Source: §B.3 · pp. 20–21

C PRIMARY DISTRIBUTIONS, GENERALITY, AND RECIPE BOUNDARIES

  • Across primary retrainings, solve and disclosure were not detectably correlated (Pearson r ≈−0.03); the second Qwen experiment had hierarchical disclosure estimate τ̂ = 0.949 [0.613, 1.266].Source: C PRIMARY DISTRIBUTIONS, GENERALITY,… · p. 21

C.1 PRIMARY RETRAININGS: ROBUSTNESS TO EVALUATION NOISE AND PROBE SELECTION

The primary-run disclosure spread remains after accounting for probe noise and on broader capability and failure evaluations. Boundary experiments extend the pattern to shortest-path and stabilized PPO, with limits on how directly those comparisons can be interpreted.

C.1 PRIMARY RETRAININGS: ROBUSTNESS TO EVALUATION NOISE AND PROBE SELECTION

  • At step 300, disclosure heterogeneity remains substantial after finite-probe noise adjustment (τ̂ = 0.864 [0.563, 1.129]), while solve is about 0.166; disclosure SD rises from 0.061 at step 15 to 0.185.Mean disclosure stays between 0.628 and 0.708, and step-150 ordering predicts step 300 poorly (Spearman ρ = 0.14 [−0.34, 0.56]).Source: §C.1 · p. 21, Table 13 · p. 23
  • On the full 100-prompt dev set, greedy solve ranges from 0.65 to 0.78 across runs with SD 0.045, equal to the estimated finite-sample floor.A 3090 Ti repeat gives solve SD 0.054, despite only 48% byte-identical greedy responses across GPU classes.Source: §C.1 · p. 21, Table 14 · p. 23
  • On naturally occurring failures across the full dev set, disclosure ranges from 0.13 to 0.93 (SD 0.235), and remains broad on the 80 prompts excluded from probe construction.These are descriptive rates on each run’s own failure set, not paired prompt-level effects; Table 15 identifies selected and unselected subsets.Source: Table 15 · p. 23, §C.1 · p. 24

C.2 SMALLER RECIPE AND FAMILY BOUNDARIES

  • For shortest-path, the greedy dev-set comparison gives a disclosure/solve SD ratio of 7.89 [5.20, 11.55], while the failure-heavy probe’s noise-adjusted ratio is not established.The separate probe’s solve rate is near floor, mechanically limiting its raw solve dispersion.Source: §C.2 · p. 24
  • Across eight stabilized-PPO runs, disclosure ranges from 0.673 to 0.814 with SD 0.047 versus 0.013 for solve; the lower solve regime prevents attributing the smaller absolute spread to algorithm alone.The two-seed RLOO comparison is only a descriptive boundary because its result is sample-small and execution-sensitive.Source: §C.2 · p. 24, Table 16 · p. 24

D.1 EXECUTION CONFIGURATIONS AND REPLAY CHECKS

Changing execution configuration can redirect disclosure despite a fixed seed and objective, and future rollout randomness can produce divergence from a restored mid-RL state. The section also tests a paragraph-break cue and verifier verdict as interventions at the reporting seam.

D.1 EXECUTION CONFIGURATIONS AND REPLAY CHECKS

  • Across six pre-specified 1.5B execution configurations, the configurations optimize the same objective with the same exact-arithmetic gradient, differing only in floating-point kernel shapes and reduction order.A one-step identical-state check yielded update cosine 0.99982 and relative difference 0.019, consistent with rounding-level floating-point differences.Source: §D.1 · p. 25
  • A separate Qwen2.5-14B example has step-300 disclosure values from 0.125 to 0.933 across four configurations, but combines hardware and worldsize changes with a different recipe.It is supporting evidence for execution sensitivity, not part of the main six-configuration estimate.Source: §D.1 · p. 25

D.2 CONTINUATIONS FROM SHARED MID-RL STATES

  • Across eight continuation cells from shared mid-RL states, within-cell rate SDs range from 0.07 to 0.27, showing that reporting can diverge after restoring a common parent state.The step-150 range of 0.11–0.88 is the widest cell, not the only cell with substantial divergence; task capability varies less in cells with the widest reporting variation.Source: §D.2 · p. 26, Figure 5 · p. 26, Table 19 · p. 26

E.1 PIPELINE EVIDENCE MAP

  • At the reporting seam, inserting a paragraph break raises later admission and reduces between-run spread in the primary recipe; adding a verifier verdict produces no additional tightening.The NoBreak control attributes most tightening to the paragraph cue rather than re-entry alone; the verdict raises mean admission in the group-local variant.Source: Figure 7 · p. 28, Figure 8 · p. 28

E.2 ROUTING LOCALIZATION

The routing analyses locate much of the observed stabilization in the learned paragraph-break cue rather than seam re-entry alone, while report prefixes affect admission more than failure evidence alone. Companion controls examine neutral cues and collateral credit, with limited evidence for general credit effects.

E.2 ROUTING LOCALIZATION

  • At step 300, paragraph-break insertion cuts raw admission SD from 0.156 to 0.069 in the primary recipe and 0.201 to 0.102 in the sibling recipe.Tightening exceeds the effect of seam re-entry alone and appears in all six raw-SD contrasts.Source: §E.2 · pp. 29–30, Table 21 · p. 29, Table 22 · p. 30
  • At step 300, teacher-forced break production and report entry are not distinguished in any recipe; the step-150 primary result does not repeat across related recipes.In the primary step-150 recipe, break probability variability has almost no relationship with natural disclosure (ρ = −0.01).Source: §E.2 · p. 30, Table 23 · p. 31
  • Failure evidence alone is insufficient in this interface, while a two-word prefix or the first third of the report phrase raises admission over re-entry by 0.141 or 0.167.The 7B inline format and grid-interface checks show that the initiating move can vary by lineage and response format.Source: §E.2 · pp. 30–31
  • Natural-output rider variation is descriptively assigned 70% to route entry and 23% to persistence on the raw scale, but mean-adjusted spreads do not distinguish them.The experiments cannot establish whether naturally silent failures went undetected or were detected but not reported.Source: §E.2 · p. 31

F NEUTRAL, PLEASANTRY, AND FORMULATION CONTROLS

  • The P-E2 marker A/B side effect on failure disclosure is about 3–4 percentage points, within preregistered tolerance, and does not change cue-adherence reproducibility.The phrase is associated with marker A across solved and failed examples, while the marker is independent of model outcome.Source: F NEUTRAL, PLEASANTRY, AND FORMULATION… · pp. 32–33

G COLLATERAL CREDIT AND DIRECT REWARD

  • Collateral credit can affect reporting, but the fresh Countdown and shortest-path experiments establish neither a general level effect nor a general explanation of retraining variability.Direct reward can fail once the model stops sampling the reporting action.Source: G COLLATERAL CREDIT AND DIRECT REWARD · p. 33

H REFERENCE ANCHORING ACROSS RETRAININGS

Reference anchoring reduces run-to-run failure-disclosure variability, with capability effects and the results of later continuation tests depending on setting and training history. The appendix specifies the penalty’s token scope, checks progress matching and coefficient sensitivity, and localizes the stabilizing effect.

H REFERENCE ANCHORING ACROSS RETRAININGS

  • Disclosure SD falls from 0.189 in the matched comparator to 0.089 under failure-conditional anchoring and 0.069 under all-token anchoring.Solve SD also narrows, while a matched-seed comparison finds that failure-conditional anchoring preserves 0.024 more solve accuracy than all-token anchoring.Source: H REFERENCE ANCHORING ACROSS RETRAININGS · pp. 34–35

H.1 EXACT REFERENCE TERM AND TOKEN SCOPE

  • The frozen SFT reference term penalizes sampled-token drift; failure-conditional anchoring selects active tokens in verifier-incorrect, format-valid rollouts, with a fixed denominator across arms.The two arms use the same β and per-token coefficient on different token sets, not the same total regularization budget.Source: §H.1 · p. 35

H.2 PROGRESS-MATCHED COMPARISON

  • Disclosure SD is 0.139 at the progress-matched unanchored checkpoint and 0.089 under anchoring, about 36% lower than the matched value.Slower progress explains part, but not all, of the narrowing; the post-hoc comparison does not fully separate the effects.Source: §H.2 · p. 35, Table 30 · p. 35

H.3 COEFFICIENT LADDER

  • Narrowing is established at β = 0.02 but not at β = 0.01; this sweep is a sensitivity check, not a fitted dose-response law.Source: §H.3 · p. 35, Figure 10 · p. 36

H.4 7B EXTENSION, PROVENANCE, AND INFLUENCE SENSITIVITY

  • Eight new 7B pairs independently reproduce reduced disclosure variation, and the pooled 19-pair interval excludes zero after every leave-one-run-out deletion.The extension used the same intervention and evaluation settings as the original wave.Source: §H.4 · p. 36, Table 31 · p. 36, Table 32 · p. 36

I.1 ANCHORED-HISTORY CONTINUATION AND POST-HISTORY ANCHORING

  • After an anchored history, continuing anchoring lowers pooled within-parent disclosure SD from 0.138 to 0.065; introducing it only after an unanchored history does not establish reduced variability.The KBR result is history-specific; mean disclosure is not detectably changed, while probe solve decreases by 0.043.Source: §I.1 · p. 37, Table 33 · p. 37, Figure 11 · p. 37

I.2 TOKEN-REGION LOCALIZATION

  • Failed-reasoning-only anchoring recovers the full stabilization effect, while tail and seam masks do not establish narrowing; 92–95% of measured reference drift lies before the reporting seam.The failed-reasoning-only gradient is nearly as large as the full-anchor gradient and points in nearly the same direction.Source: Table 34 · p. 38, Table 36 · p. 38, Table 35 · p. 38

J EXTENDED ROBUSTNESS AND BOUNDARY ANALYSES

J.1 TRAINING BEYOND 300 STEPS

The beyond-step-300 cases do not identify a single long-term reporting endpoint, and narrow detectors can mistake changes in wording for lost disclosure. The related-work discussion distinguishes this paper’s reproducibility question from work on recognizing, correcting, or incentivizing reports.

J.1 TRAINING BEYOND 300 STEPS

  • Beyond step 300, disclosure outcomes are mixed across runs and models, and narrow phrase detectors can mistake wording changes for loss of reporting.The authors treat their primary claim as reproducibility at a fixed training budget, not distinct stationary endpoints.Source: §J.1 · p. 40

K EXTENDED RELATED WORK

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