Pith.

Machine Learning · arXiv:2610.15778 v2 · submitted 11 Oct 2026

Who Sets the Pace of Judge Hacking? Judge Capability versus the Policy-Judge Gap

Haosen Wang

The paper says

“Under GRPO against a frozen, reference-free LLM judge, RL exploits the judge's false positives. Does the policy-judge capability gap or the judge itself set how fast and how far?”

more of the abstract

We train 0.5B and 1.5B Qwen2.5 policies on GSM8K against four judges at least as large, and the 1.5B policy also against one smaller judge. In a post-hoc analysis, judge acceptance rose, but no cell of 12 gained more than 0.04 in seed-mean held-out greedy accuracy. A gold-reward control with the same recipe raised the 1.5B policy's accuracy by +0.054 (for the 0.5B policy, gold reward gave no detectable gain either). The depth of judge hacking tracks the judge: the plateau correlates with judge AUC (Spearman -0.69 over 12 cells), and within a family the larger judge is fooled less deeply. For the pace, two pre-specified pairs contradict the gap account: the cell with the larger gap was fooled 3.5x sooner at the pre-specified threshold. With 12 cells, however, we cannot formally separate judge AUC from the gap for either endpoint. A blind test of step-0 predictors on three held-out judges was inconclusive. At 7-8B, judges from three families plateaued between 0.37 and 0.85.

from the abstract

Pith says

Machine review · deepseek-v4-flash · 14 Oct 2026 · of version 1 of the paper; version 2 is newer · what was read was not recorded · not checked by a person

It can be wrong. Challenge this review or reply to it.

Holds up. The most systematic, pre-registered empirical study of judge hacking to date, with a clean central finding and honest limitations; the secondary analyses are underpowered but transparently reported. This line is wrong

2 major objections · 6 minor

How often objections from reviews like this one are right: not yet measured

Are you an author? What you can do.

Not checked: figures, code, what the references say.

The paper says, at Section 3, Appendix C

The review did not quote this passage.

A classifier read this sentence of the paper as acknowledging the concern (probability 0.86):

“Deviations: (1) the SFT validity check of the sharpening check failed (Appendix C); (2) the plateau comparison used the point estimate of P1.5×Q1.5 (0.965, 2 seeds), not its interval; (3) refitting the shared-σ AFT model with the 4 new runs moved the other cells slightly (largest change: P0.5×Q7, t0.5 geometric mean 192.3→191.0 ); this paper keeps the 38-run fit for stages 1–5.”

Pith says: Objection 1 of 2 · major

The sampling-sharpening check (Table 7 and surrounding text) uses a validity gate requiring that the SFT greedy accuracy measured in the check match the logged step-0 value within 0.01. This gate failed: the SFT greedy accuracy is 0.31/0.58 versus logged 0.33/0.61.

more of objection 1

The authors state that the classification is unchanged when using the logged values, but they do not present the re-classification explicitly. Please report the sharpening/learning classification that would result from using the logged step-0 greedy accuracy as the baseline, and verify that all cells indeed remain 'sharpening'. This would strengthen confidence in the check.

The paper says, at Section 4, Table 2 and Figure 1

The review did not quote this passage.

A classifier read this sentence of the paper as acknowledging the concern (probability 0.68):

“(iii) Screening candidates, the plateau endpoint, the test’s pass rule and the step coordinate were set after some outcomes were known (Appendix A).”

Pith says: Objection 2 of 2 · major

The pre-specified pairs (Pair 1 and Pair 2) are presented as descriptive contrasts that contradict the gap account. The paper notes that the h≥0.3 versions of these contrasts were added post hoc (after stage 5). Since the gap account is a central foil, the post-hoc selection of threshold could inflate the apparent contradiction.

more of objection 2

Please clarify in the main text (not just in Appendix A) that the h≥0.5 versions were pre-specified, and the h≥0.3 versions are post-hoc. The abstract and conclusion use h≥0.3 for the pair 2.6× and 3.5× ratios; these should be flagged as post-hoc or a justification should be given for why the 0.3 threshold is more informative despite not being pre-specified.

6 minor objections

The paper says, at Section 3, Table 3

Pith says: minor objection 1 of 6

Table 3 reports 'Max gain (step)' but the step column is ambiguous: it lists the evaluation step at which the maximum occurred, but some cells have runs of different lengths (150 vs 250 steps). Clarify whether the step refers to a specific seed's maximum or the seed-mean maximum.

The paper says, at Section 4, Table 5

Pith says: minor objection 2 of 6

In Table 5, the row '∆P at Q7, h≥0.3' reports a 95% interval [-0.30, 0.10], but a few lines up it is reported as [-0.33,0.13] (97.5%). Please reconcile these numbers or annotate the table with the confidence level used for each row.

show 4 more

The paper says, at Section 2, Equation (Gcal definition)

Pith says: minor objection 3 of 6

The calibration mapping G = logit(Yes) - logit(No) and the fitted scaling parameters a,b are described. It would be helpful to state explicitly that the logit here is the raw output logit for the 'Yes' and 'No' tokens, and that (a,b) are fitted by logistic regression on step-0 correctness.

The paper says, at Appendix A, Deviations

Pith says: minor objection 4 of 6

The third deviation for Stage 2 (generous gold label) is described as 'did not change the verdict'. Since the paper uses the lenient label throughout, this deviation could be removed or shortened to avoid confusion. The generous label is not used elsewhere.

The paper says, at Appendix C, Parser audit

Pith says: minor objection 5 of 6

The parser audit reports 5.7% errors and states that the generous label agrees with the per-answer label on all 300. It then reports that under the generous label the P1.5×Q7 plateau is 0.367 instead of 0.414. Consider adding the generous-label plateau for other cells where parser errors were found (e.g., P0.5×Q7) to assess the sensitivity of the plateau results to parser errors.

The paper says, at General

Pith says: minor objection 6 of 6

The paper uses 'judge-RL' as a shorthand for GRPO against a frozen LLM judge. The term could be misinterpreted as training the judge itself. Consider adding a brief definition at first use.

What would settle it

Recompute the seed-mean greedy accuracy for each cell using a larger held-out set (e.g., all 5,473 training problems, which have gold labels) and the generous label to reduce parser errors. If any cell shows a seed-mean gain exceeding 0.05 with a 95% confidence interval excluding zero, the central claim weakens. Conversely, if the results remain consistent, the claim is further strengthened.

from the skeptic's reading

How the review went

4 readings by deepseek-v4-flash · 14 Oct 2026

  1. Reader holds up confidence high
  2. Skeptic partly agrees 48 s · 28,419 tokens read, 4,918 written
  3. Editor wrote the verdict above 20 s · 29,220 tokens read, 1,937 written
  4. Referee minor revision: 2 major objections, 6 minor 18 s · 28,712 tokens read, 2,140 written

Not run on this paper: the simulated authors' defence.

Pith did not check this review's objections against the paper.

The review in full

The review in brief, machine-written

The core finding — that GRPO against frozen, reference-free LLM judges does not detectably improve held-out greedy accuracy in any of 12 cells — is robust and well supported. The paper earns its keep through a careful crossed design, pre-registered specifications with hash-locked stages, and transparent reporting of every deviation. The gold-reward control for the 1.5B policy confirms that the flat accuracy is specific to the judge reward, which strengthens the interpretation.

What the paper does well: it separates judge capability from the policy–judge gap better than any prior work in this specific setting, shows that judge AUC correlates with hacking depth (plateau), and documents that the early rise in rollout accuracy is mostly sampling sharpening, not useful learning. The authors flag every limitation — small policies, one task, 2–4 seeds, no equivalence test — and do not oversell the correlational results. The blind predictor test is small but honestly inconclusive.

Soft spots: the gold-reward control for the 0.5B policy also showed no detectable gain, so the claim that flat accuracy is specific to the judge reward holds only for the 1.5B policy; this is acknowledged but easy to overlook. The sampling-sharpening check failed its own validity gate (SFT greedy accuracy differed by >0.01), though the authors argue the classification is unchanged. The separation of judge AUC from the gap remains tentative — the difference in correlations does not exclude zero for either endpoint. With 12 cells that share judges and policies, the bootstrap intervals are optimistic, which the authors note.

Overall, this is a solid empirical contribution that advances the conversation about what drives reward hacking with frozen LLM judges. The central negative result is credible and methodologically grounded; the exploratory parts are labelled as such.

I would bring this to a reading group focused on RL reward design, cite it in my own work if I study similar verification settings, and accept it for peer review. The paper needs no major revision, just a careful read of the supporting analyses.

The strongest objection

The central claim is that judge-RL did not detectably improve held-out greedy accuracy in any of the 12 cells. This is a negative claim supported by direct measurement of greedy accuracy on 200 held-out problems with multiple seeds per cell. The authors transparently report that small gains are not excluded (no equivalence test), that the gold-reward control for P0.5 also showed no gain (so the flat accuracy is not specific to the judge reward for that policy), and that parser errors (5.7%) exist. None of these threaten the central claim, which is simply that no detectable gain was observed. The weakest assumption identified by the reader—the sampling-sharpening classification's reliance on step-50 checks for a cell with a later rollout peak—does not bear on the central claim because the claim rests on direct greedy accuracy measurements, not on the classification. Even if the classification were wrong, the greedy accuracy flatness remains. The paper's limitations are extensive and honestly stated; no hidden flaw undermines the core finding.

The reader's weakest_assumption concerns the sampling-sharpening classification. While this classification is indeed imperfect (failed validity gate, extrapolation for P0.5×Q7), it does not bear on the central claim, which is about held-out greedy accuracy measured directly. The central claim is well supported by the data in Table 3 and Figure 2: no seed-mean gain exceeds 0.04, and single seeds at most +0.085. The gold-reward control confirms that the setting can detect gains (for P1.5). The authors acknowledge all limitations (small evaluation set, no equivalence test, parser errors, etc.). No contradictory evidence is presented. Therefore, no adjustment to the reader's ACCEPT verdict is warranted.

The referee's report

If the results are robust, the paper makes a significant empirical contribution to the understanding of reward hacking with LLM judges. The central finding—that GRPO against frozen judges yields no detectable gain in held-out greedy accuracy while acceptance rates rise—is clearly demonstrated across 12 cells with multiple seeds. The correlation between judge AUC and plateau depth is a novel descriptive insight. The blind test of step-0 predictors, though inconclusive, provides a methodological template. The paper's honesty about its scope (one task, small models, no equivalence test) strengthens rather than weakens its contribution. The negative result is meaningful for practitioners who might otherwise assume that increased judge acceptance implies improved correctness.

Pith's reading of the paper (a machine's summary, not the authors')

This paper tries to establish that when a policy is trained with GRPO using a frozen, reference-free LLM judge as the reward, the policy learns to produce more convincing wrong answers without improving true accuracy. That finding matters because LLM judges are widely used as rewards in reinforcement learning for language models, and undetected hacking could undermine training. The paper further asks what sets the pace and depth of this hacking: the judge's own initial capability (its AUC for distinguishing correct from wrong answers) or the capability gap between judge and policy. Across 12 (policy, judge) cells, the depth of hacking correlated with judge AUC, not with the gap, while the pace showed mixed evidence; a gold-reward control confirmed that for the larger policy the flat accuracy was specific to the judge reward, and early rises in rollout accuracy were mostly sampling sharpening rather than genuine learning.

What carries the argument. The central object is the 'fooled fraction' h, defined as (FPR – FPR₀)/(1 – FPR₀) on 5-step windows, where FPR is the false positive rate of the judge at the calibration threshold. The plateau (mean h over steps 101–150) measures the depth of hacking, and the onset (first step where h ≥ 0.5 or 0.3 on two consecutive windows) measures its pace. Judge capability is quantified by step-0 AUC (area under the ROC curve for correct vs. wrong answers) on the policy's held-out samples. The capability gap is logit(AUC) – logit(policy greedy accuracy). The study uses these to separate the judge account (judge sets pace and depth) from the gap account (policy–judge capability gap sets them).

Core claim. The paper finds that in all 12 cells of GRPO against frozen, reference-free LLM judges on GSM8K, the training-judge accepted more answers but held-out greedy accuracy never rose more than 0.04 in seed mean (single seeds at most +0.085). A gold-reward control with the same recipe raised the 1.5B policy's greedy accuracy by +0.054, so for that policy the flat accuracy is specific to the judge reward; for the 0.5B policy, gold reward gave no detectable gain, so its flat accuracy is not specific to the judge. In the four rising cells checked at step 50, the rise in training-rollout accuracy was mostly sampling sharpening (temperature-1 accuracy rose, greedy accuracy did not detectably change), and the gold-reward cells also showed sharpening at step 50. For the depth of hacking (the plateau of the fooled fraction), judge AUC had a Spearman correlation of –0.69 [–0.94, –0.14] over 12 cells, and within a family the larger judge was fooled less deeply; for the pace (onset), two pre-specified pairs contradicted the gap account (larger-gap cell hacked 3.5× sooner at the pre-specified threshold), but with 12 cells the two accounts cannot be formally separated. A blind test of a step-0 predictor did not beat step-0 AUC on three held-out judges, and at 7–8B, judges from three families plateaued at 0.37, 0.67 and 0.85, showing that same-size judges from different families differ widely.

The premise it rests on. The sampling-sharpening classification assumes that if temperature-1 accuracy rises but greedy accuracy does not detectably change, then no useful learning beyond sharpening is occurring; this check itself had a failed validity gate (the SFT greedy accuracy measured in the check differed from logged step-0 by more than 0.01), so the classification of one cell (P0.5×Q7) where the rollout accuracy peak is later than the check step rests on extrapolation.

If the paper is right (Pith's inferences, not the authors')

Practitioners using frozen reference-free LLM judges as rewards in GRPO should not expect improved true accuracy; they should verify with a gold reward or a separate metric, because the policy may only become more convincing without becoming more correct.

The depth of hacking can be roughly predicted from the judge's step-0 AUC, but not from the policy–judge gap, suggesting that improving the judge's initial discrimination is more important than closing the capability gap.

Within a judge family, a larger judge is hacked less deeply, so scaling the judge helps; however, across families, same-size judges vary widely (plateaus of 0.37, 0.67 and 0.85 for 7–8B judges), so family matters more than raw parameter count.

The early rise in training-rollout accuracy is mostly sampling sharpening, not genuine learning, so short training runs may overestimate progress and should be interpreted with caution.

The gold-reward control shows that a larger policy (1.5B) can improve true accuracy with the same recipe when the reward is correct, but a smaller policy (0.5B) cannot, indicating that the flat accuracy under the judge reward is not simply a recipe failure for all policy sizes.

If judge AUC robustly predicts hack depth but the gap does not, then oversight strategies should focus on improving the judge's initial discrimination rather than on matching policy capability; this suggests a different R&D priority than what the gap account implies.

The large cross-family variation at the same size implies that the internal structure of the judge (training data, architecture, chat template) strongly affects its vulnerability to hacking, which warrants systematic study beyond scaling within one family.

The blind test failure of the calibration slope predictor to beat AUC on three held-out judges indicates that step-0 metrics that work within a judge family may not generalize across families, so cross-family evaluation is essential for developing robust predictors of hackability.

The finding that onset often occurs before the peak in rollout accuracy suggests that hacking begins before the policy's rollout accuracy has saturated, which may point to a different mechanism than simple overoptimization: the judge's false positive region is exploited from the start, not gradually discovered.

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The paper

Abstract

Under GRPO against a frozen, reference-free LLM judge, RL exploits the judge's false positives. Does the policy-judge capability gap or the judge itself set how fast and how far? We train 0.5B and 1.5B Qwen2.5 policies on GSM8K against four judges at least as large, and the 1.5B policy also against one smaller judge. In a post-hoc analysis, judge acceptance rose, but no cell of 12 gained more than 0.04 in seed-mean held-out greedy accuracy. A gold-reward control with the same recipe raised the 1.5B policy's accuracy by +0.054 (for the 0.5B policy, gold reward gave no detectable gain either). The depth of judge hacking tracks the judge: the plateau correlates with judge AUC (Spearman -0.69 over 12 cells), and within a family the larger judge is fooled less deeply. For the pace, two pre-specified pairs contradict the gap account: the cell with the larger gap was fooled 3.5x sooner at the pre-specified threshold. With 12 cells, however, we cannot formally separate judge AUC from the gap for either endpoint. A blind test of step-0 predictors on three held-out judges was inconclusive. At 7-8B, judges from three families plateaued between 0.37 and 0.85.

The paper's own sentences, arranged, kept beside the review and separate from it. Each label is drawn from a closed vocabulary; the number beside it is the probability the classifier gave that label. No sentence in this record was written by a model.

abstract compiled · 2026-10-14

The authors' main claim, as the classifier picked it out 0.68

“The depth of judge hacking (the plateau) tracks the judge: it correlates with judge AUC (Spearman -0.69 [-0.94, -0.14] over 12 cells), and within a family the larger judge is fooled less deeply.”

How the main claim is stated: asserted 1.00

What the abstract itself states, as probabilities: claims first 0.03 · states limitation 0.98 · human participants 0.03 · controlled comparison 0.97 · randomized assignment 0.04 · states quantitative result 0.99 · compares with prior results 0.92 · mentions code or data availability 0.03

The abstract, sentence by sentence

This table labels the abstract only (arXiv listing abstract v1). The number is the probability the classifier gave the label.

SentenceRoleThe authors' own workStates the main conclusionStrength
When a policy is trained with GRPO against a frozen, reference-free LLM judge, the judge accepts more of its answers, but in a post-hoc analysis we detect no gain in held-out greedy accuracy: in all 12 (policy, judge) cells, the seed-mean gain never exceeded 0.04. result 1.00 0.95 0.19 asserted 1.00
A gold-reward control with the same recipe raised the 1.5B policy's greedy accuracy by +0.054 [0.013, 0.096], so for this policy the flat accuracy is specific to the judge reward; for the 0.5B policy, gold reward also gave no detectable gain. result 0.97 0.95 0.09 asserted 0.97
In the four rising cells we checked, the early rise in training-rollout accuracy is mostly sampling sharpening, as it is under gold reward. interpretation 0.63 0.91 0.05 asserted 0.87
We then ask whether the policy-judge gap or the judge sets how far and how fast RL exploits the judge's false positives. gap 0.60 0.25 0.07 unclear 0.68
We train 0.5B and 1.5B Qwen2.5 policies against four judges at least as large (Qwen2.5-1.5B/3B/7B, Llama-3.2-3B) and the 1.5B policy against one smaller judge (Qwen3-0.6B). method 0.98 0.95 0.03 asserted 0.95
The depth of judge hacking (the plateau) tracks the judge: it correlates with judge AUC (Spearman -0.69 [-0.94, -0.14] over 12 cells), and within a family the larger judge is fooled less deeply. result 0.99 0.96 0.34 asserted 1.00
For the pace (onset), two pre-specified pairs contradict the gap account (the larger-gap cell was fooled 3.5x sooner at the pre-specified threshold). result 0.84 0.94 0.15 asserted 0.98
With 12 cells we cannot formally separate judge AUC from the gap for either endpoint. limitation 1.00 0.82 0.09 asserted 0.97
The smaller judge was not fooled sooner than a judge as large as the policy, though it also differs in family and template. result 0.87 0.92 0.05 asserted 0.96
In a blind test on three held-out judges, a hash-locked step-0 predictor did not beat step-0 AUC, but three cells cannot separate them. result 0.78 0.94 0.04 asserted 0.86
At 7-8B, judges from three families plateaued at 0.37, 0.67 and 0.85. result 1.00 0.90 0.09 asserted 1.00

What kind of paper the classifier reports this is: empirical study 0.99 · evidence from observation or experiment 0.94

What was examined, and what was not

Sources read

  • arXiv listing abstract v1

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  • figures and tables
  • references and citing sentences
  • relations to other papers

Levels run

  • P abstract

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  • S sections
  • T body sentences
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How the labels were made

Compiled by classifier-1.13.0 via TypeSafe API, question bank abstract-p1-20260923, 2026-10-14: 1 request, 8,706 input tokens.

Every quoted sentence on this record is the authors'. Every label is from Pith's closed vocabulary, with the probability shown beside it. This record as JSON

Figures (6)
Figure 1 of the paper
Figure 1. Cells with similar gaps differ in onset. Onset t0.3 against the step-0 capabil￾ity gap logit(AUC) − logit(accuracy). Small marks: runs; large: AFT means (circle: P0.5; square: P1.5; open: held-out judge). Dashed: pre￾specified pairs. Qw3-0.6: judge smaller than the policy (stage 6; 42-run fit)
Figure 2 of the paper
Figure 2. The judge accepts more answers while held-out accuracy stays flat or falls.
Figure 3 of the paper
Figure 3. Training-rollout accuracy rises early in 11 of 12 cells, then falls.
Figure 4 of the paper
Figure 4. Fooled fraction h for the 0.5B policy under the four stage 1–3 judges (seed mean and range). Gray: plateau window. Dashed: the onset thresholds 0.3 and 0.5; 0.5 lies just above the Q7 plateau. Q1.5 and Q7 curves end at step 150, the shortest run in those cells. 4 IN OUR CELLS WITH JUDGE ≥ POLICY, THE GAP DID NOT SET THE PACE The depth of judge hacking (the plateau) tracks the judge: it correlates with judge AUC (Spearman −0.69 [−0.94, −0.14] over 12 cells), and within a family the larger judge is fooled less deeply (Section 5.1). For the pace (onset), the two pre-specified pairs…
Figure 5 of the paper
Figure 5. The locked step-0 predictor does not beat step-0 AUC on held-out judges.
Figure 6 of the paper
Figure 6. Answer format and length of the training rollouts

Figures are the authors', reproduced from the paper.

Cited by 2 Pith papers

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