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Artificial Intelligence · arXiv:2610.18760 v1 · submitted 13 Oct 2026 · 69 references

Beyond the Verdict: Agentic Code Judging with Verifiable Feedback

Zheye Deng, Sha Li, Changlong Yu, Xin Liu, Qin Lu, Priyanka Nigam, Yangqiu Song

The paper says

“Test-time scaling for large language models (LLMs) can involve generating multiple candidate solutions for selection or revising an earlier attempt. To guide selection and revision, we need a verifier that can estimate candidate correctness and provide evidence of failure.”

more of the abstract

In competitive programming, however, official judging systems provide authoritative verdicts under finite submission budgets, without revealing failure explanations or failing inputs. To provide informative feedback without consuming official submissions, we formulate a task in which a model judges and diagnoses a candidate program using only the problem statement and source code, with generated counterexamples serving as checkable evidence. To evaluate this task, we build USACO-JUDGE from the USACO 2026 contests, using accepted and unaccepted programs written by human experts and multiple LLMs. We then train ARBITER, a 35B mixture-of-experts (MoE) agentic verifier, with reinforcement learning in a generic execution sandbox. Training raises counterexample success on incorrect programs from 40.61% to 62.67% and mean binary verdict accuracy on USACO-JUDGE from 71.41% to 87.41%, approaching frontier verification performance. Beyond verification, ARBITER outperforms baselines in both code selection and refinement. In an IOI 2026 case study, ARBITER-guided refinement raises GPT-OSS-120B's expected score above the gold-medal threshold under the official submission limit.

from the abstract

Pith says

Machine review · deepseek-v4-flash · 14 Oct 2026 · what was read was not recorded · not checked by a person

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

Holds up, with conditions. Serious empirical paper on agentic code verification with checkable counterexamples; the central training claim holds up, and the real risk is the self-built judge oracle, not the table readings. This line is wrong

2 major objections · 7 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 69 references say.

The paper says, at §5.2, Appendix B.3, Appendix A, Figure 3

The review did not quote this passage.

Pith says: Objection 1 of 2 · major

The headline counterexample-success numbers (40.61% to 62.67%) and the Figure 3 training reward both flow through the same in-house oracle: hand-written validators for all 39 USACO problems, custom output checkers for six, and reference solutions. The statement that validators and checkers are 'verified end to end' means they reproduce official verdicts on the official test data, which is not an audit of their behavior on novel generated inputs.

more of objection 1

A validator that admits illegal inputs, a reference solution with a bug, or a custom checker that misjudges a valid output would inflate training reward and evaluation labels at the same time, and reinforcement learning could in principle exploit such a loose oracle beyond what a single-shot baseline would do. The verdict-accuracy claims (71.41% to 87.41%) are far less exposed because they rest on rejudged official test data whose original scores are reproduced, so the residual risk is specific to the hack protocol. The mitigating evidence is real: UOJ-BENCH re-hosting reproduces original outcomes, the 400-case human audit was unanimous, the QOJ 390.20 realization is independent of the authors' oracle, and Appendix D.6 documents two hand-verifiable hacks of officially accepted submissions. None of this, however, re-checks a random sample of successful USACO-JUDGE counterexamples against an independent implementation. I request a manual audit of a random sample of successful hacks (input legality against the problem statement and genuineness of the induced failure under the intended judging semantics), plus an explicit statement of this residual risk in Section 5.2.

The paper says, at §6.2, Appendix F.2, Figure 1

The review did not quote this passage.

Pith says: Objection 2 of 2 · major

The 385.46 versus 334.6 contrast in Figure 1 and the Introduction is attributed to verifier feedback versus online-judge feedback, but the two policies differ in exploration as well: the ARBITER condition starts 50 internal trajectories with free verifier reviews, while the judge condition runs 10 trajectories with at most five judge queries each, both under the same 50-submission cap.

more of objection 2

The appendix discloses the trajectory counts, which I credit, but no matched-trajectory control is reported and the abstract and Figure 1 framing do not carry the caveat. The absolute claim is well supported: 385.46 is above the 361.12 gold threshold and is bracketed by the realized 390.20 on QOJ (Appendix F.2). The fix is therefore local: either add a judge-condition arm with 50 trajectories and one submission each (or an ARBITER arm with 10 trajectories), or reframe Figure 1 as a policy-level comparison rather than a feedback-type ablation.

7 minor objections

The paper says, at Table 1

Pith says: minor objection 1 of 7

The two USACO-JUDGE column groups appear to be swapped relative to their labels: the advertised 71.41/87.41 verdict-accuracy averages and the 65.34/84.50 hard-split values quoted in Section 6.1 reproduce only when the columns labelled 'Hack Succ.' and 'Verdict Acc.' are exchanged for the USACO half of the table. The underlying data are consistent; the labels must be fixed.

The paper says, at Table 1

Pith says: minor objection 2 of 7

The 'Overall Hack Succ.' column is not recoverable from the split-level values in Table 1 and the funnel in Table 7: candidate-weighted averages of the corrected split rates give approximately 42.5 and 65.4 for the agentic Qwen baseline and ARBITER, versus the reported 40.61 and 62.67. Please state explicitly how the overall is pooled, including how officially Accepted candidates that are hacked enter the numerator and denominator.

show 5 more

The paper says, at §4.1

Pith says: minor objection 3 of 7

Please state explicitly whether 'exclude all evaluation problems' covers the UOJ-BENCH problem set; since the training rollouts are online-judge-graded across 6,145 problems and UOJ-BENCH is UOJ-based, problem-level overlap with the training pool would inflate the UOJ-BENCH results even though the released candidates are excluded.

The paper says, at §6.1, Table 1

Pith says: minor objection 4 of 7

The headline verification figures are point estimates without dispersion; the selection study reports ranges over repeats, and the same treatment (or confidence intervals) should be given to the verdict-accuracy and hack-success numbers and to the expected IOI scores.

The paper says, at §6.1, Table 1

Pith says: minor objection 5 of 7

Given the 1:2 accepted/unaccepted ratio of USACO-JUDGE, an always-unaccepted baseline achieves 66.7% verdict accuracy; stating this floor next to the 71.41/87.41 figures would put the reported gain in context.

The paper says, at §6.3, Table 3

Pith says: minor objection 6 of 7

Comparisons against published baselines use regenerated pools with unmatched inference compute, as the paper acknowledges; because pool difficulty can differ even when aggregate uniform-selection rates match, the same-pool comparison against the perfect-selection bound is the strongest evidence, and the cross-pool baseline comparisons should be labeled as suggestive.

The paper says, at Figure 3

Pith says: minor objection 7 of 7

The caption and reward annotations are garbled in the submitted text ('+0.05runs +0.10legal +0.750breakssurvives' and similar); the reward decomposition needs a clean, legible rendering.

What would settle it

Have two independent competitive programmers, or the USACO problem setters, re-implement the 39 input validators and six custom checkers from the official problem statements without seeing the authors' code, then replay every successful ARBITER counterexample in USACO-JUDGE, including the Appendix D.6 hacks of officially Accepted submissions. Recompute hack success and the 71.41/87.41 verdict accuracy using only hacks that pass the independent validator and fail under the independent checker; any mismatch with the in-house UOJ results quantifies the inflation, while a clean replay would settle the concern.

from the skeptic's reading

How the review went

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

  1. Reader holds up, with conditions confidence moderate
  2. Skeptic agrees 2 min 25 s · 32,670 tokens read, 21,530 written
  3. Editor wrote the verdict above 36 s · 33,652 tokens read, 4,798 written
  4. Referee major revision: 2 major objections, 7 minor 3 min 11 s · 32,942 tokens read, 30,556 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

Short version: this is one of the more careful empirical papers I have seen in this area. The new thing is the integrated task—verdict plus diagnosis plus deterministic replayable counterexample for a single candidate—trained end-to-end with execution-grounded rewards, and evaluated on USACO-JUDGE, a balanced benchmark with accepted and unaccepted programs. The training gains are real on their own terms: counterexample success on incorrect programs goes from 40.61% to 62.67%, and the candidate-weighted USACO verdict accuracy from 71.41% to 87.41%. I checked the reader's column-order worry: it does not land. Those figures reproduce from Table 1 as weighted averages of the USACO verdict columns, so the abstract is not misreporting the table. The evaluation design earns real credit: rejudged labels, validators and custom checkers exercised end to end, a verification funnel, a 400-case human audit with unanimous labels, and honest diagnostics of the majority-class shortcut and length-control side effects. The IOI case study is presented as an expected score, not a realized run, and the appendix discloses the trajectory-count asymmetry; the separate QOJ realization of 390.20 partly mitigates the worry.

The soft spot that matters is oracle fidelity. Every training reward and every headline metric flows through the authors' own UOJ re-host, with hand-written validators for all 39 USACO problems and custom checkers for six. Reproducing a candidate's original score verifies that the re-host agrees with official judging on existing tests; it does not independently validate behavior on novel generated inputs. A bug in a validator or checker would inflate training signal and evaluation numbers at the same time. The human audit and the QOJ run are mitigating evidence, but they do not re-audit the USACO-JUDGE hack protocol. This is not a fatal flaw, but absolute numbers will only be credible after independent validation of a sample of the validators or third-party judging of counterexamples. Two smaller issues: the selection comparison uses published baselines on regenerated pools with unmatched inference compute, and no error bars accompany the headline deltas. Both are disclosed, but they make the precise cross-system gaps weaker than the tables suggest. The central direction—that executable-reward RL on an agentic judge improves both selection and refinement feedback—holds up. This paper deserves a serious referee. If you work on code verifiers or test-time scaling, it is worth your time and worth citing after the oracle question gets an independent check.

The strongest objection

Every training reward and evaluation label flows through the paper's UOJ re-host, and the oracle is not independent of the method. For USACO-JUDGE, input validators for all 39 problems and output checkers for six multi-output problems are hand-written by the authors (Appendix B.3). The reward in Figure 3 pays +0.75 for an input that breaks the candidate and +0.10 for overturning an officially Accepted verdict; the same in-house check decides whether an Accepted candidate is re-labelled unaccepted in Section 6.1. A validator that admits illegal inputs, a reference solution with a bug, or a custom checker that misjudges an output would simultaneously inflate the training signal and the headline 40.61% to 62.67% and 71.41% to 87.41% numbers. The claim that validators and checkers are 'verified end to end' is an assertion, not an audit; reproducing a candidate's original score on official tests does not validate a checker on novel generated inputs. The external QOJ realization (390.20) and the 400-case human audit are real mitigating evidence, but they do not re-check the USACO-JUDGE hack protocol. The reader's Table 1 column-order concern does not land: the advertised 71.41/87.41 figures reproduce exactly as candidate-weighted averages of the USACO verdict columns (85.56/65.34 and 94.20/84.50 over 270/630 candidates), so the oracle question is the one that controls the central claim.

The central claim is that execution-grounded RL training produces a verifier whose checkable counterexamples improve both verdict accuracy and downstream refinement. For that claim to hold, the judge-side checks that produce the reward and the evaluation labels must faithfully implement the contest's judging semantics. This is the weakest link because the same in-house oracle sits on both sides: it validates generated inputs, runs the candidate and reference solution, compares outputs, and even re-labels officially Accepted candidates when a counterexample succeeds. A bug in any of those components would not just add noise; it would systematically reward and measure the same false signal, so the reported deltas could survive internal consistency checks while failing to transfer to official judging. The paper reports careful end-to-end verification of validators and checkers, an external QOJ score for the IOI case study, and a human audit, all of which are real support, but none independently re-audits the USACO-JUDGE oracle on model-generated counterexamples. I do not claim the oracle is in fact buggy; I claim it is the assumption that must be independently checked before the headline numbers can be read as evidence about real contest semantics. Since the reader already identified this as the weakest assumption and built a CONDITIONAL verdict on it, my read does not change the verdict: it stays conditional pending independent oracle validation.

The referee's report

The paper is careful and unusually honest about its own failure modes: the majority-class-guessing diagnostic (Appendix G.1), length-control side effects (G.3), the false-positive penalty trade-off (G.2), and the expected-versus-realized IOI accounting (F.2) are all disclosed and analyzed. The evaluation apparatus is a strength: USACO-JUDGE labels are rejudged with reproduced original scores, UOJ-BENCH is re-hosted and reproduces original outcomes, the verification funnel (D.3) localizes where attacks succeed or die, and the 400-diagnosis human audit reached unanimous labels. The headline verdict-accuracy figures are internally consistent: 71.41 and 87.41 reproduce exactly as candidate-weighted averages of the split-level USACO-JUDGE columns once the Table 1 column labels are read correctly, and the overall hack-success figures are consistent with the split-level funnel data in expectation. The QOJ 390.20 realization of the IOI case study provides an independent check of the absolute claim.

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

This paper tries to establish that an LLM can be trained to act as a judge for competitive-programming solutions: given only the problem statement and a candidate program, the model must predict whether the program survives the hidden official tests, say why it fails when it does, and return a concrete failing input that anyone can run and check. That matters because official judges spend a finite submission budget and return only a verdict, while test-time scaling—generating many candidates or revising a faulty attempt—needs cheap feedback that does not consume that budget. The authors train ARBITER, a 35B mixture-of-experts verifier, with reinforcement learning in an execution sandbox, rewarding it mainly for counterexamples that pass an input validator and actually break the candidate. Training raises counterexample success on incorrect programs from 40.61% to 62.67% and mean binary accept/reject accuracy on their new USACO-JUDGE benchmark from 71.41% to 87.41%; in an IOI 2026 case study, ARBITER-guided refinement lifts an open 120B solver to an expected 385.46 points, above the 361.12 gold threshold, under the official 50-submission cap. If the claims hold, a comparatively small verifier can supply the evidence needed for both choosing among solutions and repairing them, without spending scarce official submissions.

What carries the argument. The load-bearing object is the episode interface and the evidence gate built around it. The verifier's final call is \texttt{submit}($v, d, g$): a verdict among Accepted, Wrong Answer, Time Limit Exceeded, Runtime Error, Memory Limit Exceeded, and Compile Error; a free-text diagnosis; and, for any non-Accepted verdict other than Compile Error, a deterministic Python 3 generator whose stdout is exactly one input. The judge withholds the hidden tests, reference solution, validator, checker, and even the result of checking the verifier's own counterexample, so the model must build its evidence inside the sandbox, by compiling, running, differential-testing, and stress-testing the candidate. The reward design carries the argument: agreeing with an unaccepted reference verdict earns only 0.05 of the 1.00 available, running the generator adds 0.05, a legal input 0.10, a validated input that breaks the candidate 0.75, and matching the failure type the final 0.05, with an extra 0.10 for overturning an officially accepted verdict—a deliberately asymmetric gate, because a counterexample can prove failure while the absence of one cannot prove acceptance. The paper reports that this proxy is meaningful: counterexamples succeed for 71.6% of human-rated correct diagnoses and only 10.3% of incorrect or vacuous ones, and an alternating adaptive length penalty keeps the trained policy from drifting into unboundedly long rollouts.

Core claim. The central claim is that verification with a replayable counterexample is a trainable task, and that a model trained to reward only executable evidence becomes a useful substitute for a large share of official judge feedback. ARBITER takes a problem statement $P$ and a candidate program $C$, runs Python and shell commands in a sandbox to test $C$ on inputs it constructs itself, then ends its episode with a triple $(v, d, g)$: a verdict, a natural-language diagnosis, and a deterministic Python generator for one input. An external judge then runs $C$ on the official tests for the reference verdict $v^\star$; if $g$ is supplied, it validates the generated input against the problem constraints, runs a reference solution, and applies the output checker, and only a legal input that breaks $C$ counts as a verified failure. Reinforcing this with reinforcement learning—a small reward (0.05 of 1.00) for agreeing on an unaccepted verdict but the bulk of the credit (0.75) reserved for a breaking counterexample—raises counterexample success from 40.61% to 62.67% overall and mean binary verdict accuracy on USACO-JUDGE from 71.41% to 87.41%, and on the hard splits brings the 35B model past non-agentic verifiers up to 1.6T parameters. The same verifier outperforms published baselines in selecting among regenerated candidate pools and, in the IOI 2026 case study, guides an open 120B solver to an expected 385.46 points versus 334.6 with online-judge feedback; the appendix discloses that the two comparison arms differ in the number of internal refinement trajectories and that ARBITER's reviews use no submission slots, an asymmetry the abstract's headline does not state.

The premise it rests on. The entire argument assumes the authors' re-hosted online judge faithfully reproduces official contest judging: a validator-approved input that breaks a candidate under their hand-written validators and custom checkers is taken to certify the candidate's failure, and that same oracle computes both every training reward and the headline metrics, so a single buggy validator or checker would inflate all reported numbers at once.

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

A trained verifier of this kind can supply the feedback that test-time scaling needs—picking among generated candidates and revising failed attempts—without consuming any official submission budget, since ARBITER's reviews use no judge slots.

The evidence gate converts diagnosis quality into a mechanically checkable training signal, so a verifier can be improved at explaining bugs without large-scale human labels.

In code selection, one ARBITER call per candidate beats the strongest published selection baseline in all eight reported settings (for example 82.6 versus 73.7 pass@1 for a 30B solver on LiveCodeBench with pools of 64), and eight calls move closer to the perfect-selection upper bound.

Officially accepted programs are not beyond suspicion: ARBITER broke USACO submissions that scored 100 on official tests, one through a quadratic cleanup loop that times out on a legal 200,000-element input and one through a sentinel collision that yields a wrong answer.

In refinement, the verdict-plus-diagnosis condition beats verdict-plus-counterexample in ten of twelve settings, indicating that the natural-language diagnosis, not the counterexample source, carries most of the repair signal.

Editorial inference: if the oracle-fidelity assumption holds, the same evidence-gated recipe should transfer to any setting where a candidate artifact can be executed against a checkable oracle and authoritative evaluations are rationed—unit-test generation, proof scripts checked by a trusted kernel, or data-pipeline validation—because the mechanism is not specific to competitive programming.

Editorial inference: the reward asymmetry the authors build in (a counterexample proves failure, its absence proves nothing) suggests learned verifiers will always be better at pruning bad candidates than at certifying good ones, so downstream systems should treat an Accepted verdict as a ranking signal rather than a guarantee; the paper's fallback to uniform selection when nothing is Accepted is

Editorial inference: a testable extension is to measure whether counterexample-grounded reinforcement learning continues to scale with backbone size and sampling budget, since the paper's curves show one ARBITER sample beating eight samples of the untrained backbone on every split, leaving open the question of where the remaining gap to frontier verifiers goes.

Editorial inference: because ARBITER found bugs inside officially accepted submissions, running it over the accepted history of a fixed contest would quantify how often official acceptance is fragile, a cheap audit the paper does not perform.

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The paper

Abstract

Test-time scaling for large language models (LLMs) can involve generating multiple candidate solutions for selection or revising an earlier attempt. To guide selection and revision, we need a verifier that can estimate candidate correctness and provide evidence of failure. In competitive programming, however, official judging systems provide authoritative verdicts under finite submission budgets, without revealing failure explanations or failing inputs. To provide informative feedback without consuming official submissions, we formulate a task in which a model judges and diagnoses a candidate program using only the problem statement and source code, with generated counterexamples serving as checkable evidence. To evaluate this task, we build USACO-JUDGE from the USACO 2026 contests, using accepted and unaccepted programs written by human experts and multiple LLMs. We then train ARBITER, a 35B mixture-of-experts (MoE) agentic verifier, with reinforcement learning in a generic execution sandbox. Training raises counterexample success on incorrect programs from 40.61% to 62.67% and mean binary verdict accuracy on USACO-JUDGE from 71.41% to 87.41%, approaching frontier verification performance. Beyond verification, ARBITER outperforms baselines in both code selection and refinement. In an IOI 2026 case study, ARBITER-guided refinement raises GPT-OSS-120B's expected score above the gold-medal threshold under the official submission limit.

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 0.77

“Beyond verification, ARBITER outperforms baselines in both code selection and refinement.”

How the main claim is stated: asserted 1.00

What the abstract itself states, as probabilities: claims first 0.06 · states limitation 0.22 · human participants 0.14 · controlled comparison 0.91 · randomized assignment 0.02 · states quantitative result 0.99 · compares with prior results 0.95 · mentions code or data availability 0.08

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
Test-time scaling for large language models (LLMs) can involve generating multiple candidate solutions for selection or revising an earlier attempt. background 1.00 0.05 0.02 hedged possibility 0.63
To guide selection and revision, we need a verifier that can estimate candidate correctness and provide evidence of failure. background 0.82 0.07 0.03 asserted 1.00
In competitive programming, however, official judging systems provide authoritative verdicts under finite submission budgets, without revealing failure explanations or failing inputs. gap 0.51 0.06 0.02 asserted 1.00
To provide informative feedback without consuming official submissions, we formulate a task in which a model judges and diagnoses a candidate program using only the problem statement and source code, with generated counterexamples serving as checkable evidence. method 0.55 0.70 0.07 asserted 0.97
To evaluate this task, we build USACO-JUDGE from the USACO 2026 contests, using accepted and unaccepted programs written by human experts and multiple LLMs. method 0.90 0.96 0.03 asserted 1.00
We then train ARBITER, a 35B mixture-of-experts (MoE) agentic verifier, with reinforcement learning in a generic execution sandbox. method 0.97 0.95 0.05 asserted 0.99
Training raises counterexample success on incorrect programs from 40.61% to 62.67% and mean binary verdict accuracy on USACO-JUDGE from 71.41% to 87.41%, approaching frontier verification performance. result 1.00 0.96 0.27 asserted 1.00
Beyond verification, ARBITER outperforms baselines in both code selection and refinement. result 1.00 0.92 0.32 asserted 1.00
In an IOI 2026 case study, ARBITER-guided refinement raises GPT-OSS-120B's expected score above the gold-medal threshold under the official submission limit. result 1.00 0.92 0.31 asserted 1.00

What kind of paper the classifier reports this is: method or tool 1.00 · evidence from observation or experiment 0.96

What was examined, and what was not

Sources read

  • arXiv listing abstract v1

Not examined

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

Levels run

  • P abstract

Not run

  • S sections
  • T body sentences
  • C citations
  • R cross-paper relations

How the labels were made

Compiled by classifier-1.13.0 via TypeSafe API, question bank abstract-p1-20260923, 2026-10-14: 1 request, 7,038 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 (9)
Figure 1 of the paper
Figure 1. Comparison of ARBITER with an online judge (left) and the IOI 2026 case study (right). Under the same 50-submission cap per problem, the expected ARBITER score crosses the gold threshold in round 4; the expected online-judge-feedback score remains below it. Test-time methods allow language models to continue working after an initial answer. They can generate several candidates for selection or revise an earlier attempt (Snell et al., 2025; Shinn et al., 2023; Venkatraman et al., 2025). Each use of additional computation depends on feedback about a candidate already produced.…
Figure 2 of the paper
Figure 2. A verification instance. The verifier’s answer and the judge-side evaluation are shown in order; judge-only
Figure 3 of the paper
Figure 3. The verification pipeline assigns partial rewards according to each outcome and combines them into the final
Figure 4 of the paper
Figure 4. Reward ablations. Left: reward, verdict accuracy, and tool use under verdict-only training. Right: Accepted precision and recall for false-positive penalties λ = 0 and 0.5. 4.3 EFFICIENT TRAINING THROUGH LENGTH CONTROL As responses grow longer during training, generation cost rises and rollout throughput falls. Inspired by length control (Kimi Team, 2026), we design an adaptive penalty. When the penalty is active, we penalize a rollout only if it earns at least 0.9 raw reward, exceeds a group-relative length threshold, and at least one-quarter of the group shares the top reward.…
Figure 5 of the paper
Figure 5. Adaptive length control. The panels compare mean reward, response length, and abort rate across two runs
Figure 6 of the paper
Figure 6. USACO-JUDGE composition by difficulty, verdict, failure type, and official score band. The USACO website provides the problem statements, test data, and official solutions, but not the validators and checkers required to deploy the problems on our own online judge. We employ experienced competitive programmers to implement validators compatible with UOJ for every problem, allowing the judge to verify that each generated input satisfies the problem constraints. For output judging, we use UOJ’s native checker whenever possible and write custom checkers for the six problems that allow…
Figure 7 of the paper
Figure 7. Test-time scaling on the Qwen3.6-35B-A3B backbone. We draw eight samples per candidate and report
Figure 8 of the paper
Figure 8. Human audit of ARBITER diagnoses. Counterexample success tracks correctness (Left), while correct diagnoses usually locate the bug and over half suggest a fix (Right). 6.2 CODE REFINEMENT For each of the 39 held-out USACO 2026 problems, we test Qwen3.6-35B-A3B and GPT-OSS-120B using eight shared, already judged starting programs and up to eight revisions. We compare previous code alone, online-judge feedback (verdict and subtask score), and three combinations of ARBITER’s verdict (V), diagnosis (D), and coun￾terexample generator (X). Round 0 is excluded from the…
Figure 9 of the paper
Figure 9. Pass@1 as ARBITER calls per candidate increase from one to eight. Rows show candidate pools of 8 and 64. Uniform and perfect selection mark the lower and upper reference levels. F REFINEMENT AND DIAGNOSIS ANALYSIS F.1 SUBMISSION PROTOCOL Round 0 is the shared, already judged starting program. It is excluded from the budget of additional submissions. Every condition retains a 100-point starting program without further submissions; only the Online Judge condition receives its result as solver feedback. For trajectories still active under Best@1, the previous-code condition refines…

Figures are the authors', reproduced from the paper.

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