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Paper summary
The paper studies single-candidate code verification: given a programming problem and a candidate solution, a verifier predicts acceptance and provides a diagnosis and a counterexample generator.
Critical strengths
A useful evaluation setup for code verification. USACO-JUDGE includes both accepted and unaccepted programs, enabling evaluation of acceptance decisions alongside counterexample discovery.
Substantial improvement over the same backbone with the agentic scaffold. The reported increase in USACO-JUDGE verdict accuracy from 71.41% to 87.41% supports the practical effectiveness of the training recipe.
Critical weaknesses
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Limited novelty. [1] already uses multi-turn code execution and GRPO to generate test inputs that make two programs produce different outputs (Sections 3.1–3.4, pp. 4–6). [2] also trains a test generator by rewarding correct tests that expose bugs (Section 4.1, pp. 3–4). The main steps of the proposed method therefore closely follow existing work.
The paper combines a verdict, diagnosis, and counterexample in , but does not introduce a clear new training method for this combined task. For example, the diagnosis receives no reward for being correct (Section 4.2, p. 5, lines 216–221). The experiments compare different feedback fields, but do not compare the method with an existing counterexample generator that also produces an explanation (Section 6.2 and Table 2, pp. 8–9). Although the benchmark and results are useful, the method mainly combines known ideas. It offers limited new insight into how to build better code judges.
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The reward values are not well justified. The paper gives 0.05 for a correct rejection, 0.05 for running the generator, 0.10 for a valid input, 0.75 for exposing a program failure, and 0.05 for matching the failure type (Section 4.2 and Figure 3, pp. 4–5). The authors explain why finding a real failure should receive more reward than the earlier steps. However, they do not explain how they chose these specific values, or show whether other reasonable values would work equally well.
The existing experiments do not answer this question. The verdict-only experiment shows that a model can learn to guess the majority class when 85% of training programs are incorrect (Appendix G.1, p. 26, lines 1384–1395). This supports rewarding actual evidence of failure, but does not explain why the reward should be split in the proposed way. The experiment in Appendix G.2 and Table 18 (pp. 26–27) changes a separate penalty for incorrectly accepting a program; it does not test the weights above. Since the reward is a key part of the method, the paper should explain how these values were chosen and test whether the results hold when they change. It should also compare against a simpler reward based mainly on whether a valid counterexample exposes a failure.
[1] Zeyao Ma et al. Scaling Agentic Verifier for Competitive Coding. 2026. arXiv:2602.04254.
[2] Qingyao Li et al. ATGen: Adversarial Reinforcement Learning for Test Case Generation. 2025. arXiv:2510.14635.
Questions for authors
- Does the order of ARBITER's output matters? UTGen [1] already uses generated tests to guide debugging, while Repair-R1 [2] trains test generation and bug repair together. Can you compare ARBITER’s joint training of verdict prediction, diagnosis, and counterexample generation (Sections 3–4, pp. 3–5) with a model trained only to generate counterexamples, then prompted to provide a verdict and explanation? With the same base model and similar training and inference budgets, does ARBITER give more accurate judgments or better repair results (Section 6.2, pp. 8–9)?
- How much does the reward design help? The verdict-only experiment uses training data with 85% unaccepted programs (Appendix G.1, p. 26). Does verdict-only training still fail if the two classes are balanced through sampling or reward weights? Under the same training settings, how much better is the full reward (Section 4.2 and Figure 3, pp. 4–5) than a simpler reward for producing a valid counterexample that exposes a failure?
- How was the length-penalty schedule chosen? Appendix C (p. 17, lines 864–866) says the penalty schedule was chosen manually from the reward curve. What rule and which data were used to decide when to turn it on? Since episodes that exceed the time limit are excluded from training updates (Section 4.2, p. 4, lines 187–191), how much does final verdict accuracy change with different penalty schedules (Section 4.3 and Figure 5, p. 5; Appendix G.3, p. 27)?
[1] Archiki Prasad et al. Learning to Generate Unit Tests for Automated Debugging (UTGen/UTDebug). 2025. arXiv:2502.01619.
[2] Haichuan Hu, Xiaochen Xie, and Quanjun Zhang. Repair-R1: Better Test Before Repair. 2025. arXiv:2507.22853.
4 comments
These results show that training of a verifier on verifiable verdict and counterexample rewards can improve the quality of its diagnosis and usefulness of the feedback.
Q1: Output order, alternative training and related methods
We would like to clarify that ARBITER is trained as an independent verifier that provides V, D, and X within a single agentic review. The review itself can consist of multiple rounds of reasoning and code execution.
Output order and scope. V, D, and X are three named fields in the final submit call. Before the submission, the model can analyze the code, execute tests and modify its verdict. The output order does not specify the reasoning order for the entire review. We compare the base model and ARBITER using the same submission interface in order to measure the gains from the training. The optimization of the output order is beyond the scope of this study.
Settings of UTGen [3] and Repair-R1 [4]. UTGen trains a model to generate the test inputs and expected outputs for candidate programs, and uses them for debugging and selection of candidates [3]. The applications of UTGen are relevant to Sections 6.2 and 6.3. However, we were not able to find publicly released trained UTGen weights, which prevented a fair comparison with the trained model.
Repair-R1 jointly trains test generation and program repair on code that is known to contain errors [4]. We evaluate an independent verifier on the candidates of unknown correctness. Section 6.2 fixes the Qwen3.6-35B-A3B and GPT-OSS-120B solvers to evaluate the feedback quality, while Section 6.3 selects candidates from existing ones. The direct adoption of the native workflow of Repair-R1 would change both the repair model and its training objective, thus preventing us from isolating the contribution of the verifier feedback. The joint training of the repair model is beyond the scope of this study.
Training only for counterexamples, and then prompting for verdicts and explanations. We would like to clarify the reason for the verdict supervision in the training objective. Our aim is to make the acceptance decision and search for the failure within a single agentic review for both the correct and incorrect candidates. The correct programs do not have valid counterexamples, and searching for failures within the incorrect programs can also fail. Therefore, the absence of the counterexample cannot distinguish the decision about the correctness from the suspicion of a bug, for which the evidence is not found. V, D, and X define the final feedback interface; D is requested via the prompt without a separate correctness reward. The training only for the counterexamples and obtaining V/D through the subsequent prompting is another approach, which is beyond the scope of this study.
Judgment accuracy and repair results under comparable backbones and budgets. Our experiments support two related findings. Under the same backbone and agentic scaffold, the training raises USACO-JUDGE Verdict Accuracy from 71.41% to 87.41%. With the verifier, solver, starting programs, and submission protocol fixed, V+D improves repair scores over V-only in all six combinations at @8 (Table 2). The additional evidence on diagnosis quality and repair benefits is provided in our response to W2.
W3+W4+Q2: Reward design, binary outcomes and class-balanced verdict training
We would like to clarify the reasons behind the reward allocation and additional ablations from Section 4.2. Appendix G.1 investigates the verdict-only training on the original and class-balanced data distributions; G.2 compares the full reward and binary outcome reward. The false positive penalty experiment is reported in G.3 and is not used as the evidence for the process rewards.
Reason for reward allocation. For the branches where a counterexample is required, correct rejection, successful generator execution, and input validity get 0.05, 0.05, and 0.10, respectively, for a total of 0.20. Discovery of the actual program failure earns the main reward of 0.75, and matching the failure type – 0.05. Thus, the reward distinguishes the unsuccessful attempts according to their checkable progress, rewarding most of all for the successful counterexamples. The correct acceptance gets 1.00.
Direct comparison with the simple binary reward. The new control uses only 0 or 1 as the task reward. Agreement on Accepted receives 1. For the branches where a counterexample is required, the reward is 1 if the coarse verdict classes agree, and the valid input exposes the actual failure, and 0 otherwise. The failure type predicted does not have to match the verdict returned by the hack, and there are no separate rewards for rejection, generator execution, or input validity.
With the same backbone, training data, optimization settings and 80 training steps, the results are as follows (Appendix G.2, Table 25):
| Evaluation metric after 80 training steps | Full reward | Binary reward |
|---|---|---|
| Verdict Accuracy | 78.00% | 77.50% |
| Hack Success | 59.77% | 56.02% |
| Mean output tokens per candidate | 33.36K | 35.31K |
| Successful counterexamples per million output tokens | 11.91 | 10.55 |
Using the unrounded records, the full reward improves Hack Success by 3.76 percentage points, reduces the mean output tokens by 5.52%, and creates 12.94% more successful counterexamples per million output tokens. Table 24 also shows that, over the first 80 training steps, the fraction of the groups where all 16 samples have identical raw task rewards decreases from 24.12% under the binary reward to 15.00% under the full reward, which is a relative decrease of 37.8%. The fraction is lower in every consecutive 20-step window. These results support the role of the process rewards in distinguishing the progress of unsuccessful attempts, as well as in increasing the discovery and output efficiency of the counterexamples within the training budget.
Verdict-only training after class balancing. We retain the Accepted samples and sample an equal number of unaccepted programs. Both the original-distribution and balanced variants receive a binary reward depending only on whether the coarse verdict is correct; the quality of the diagnosis and counterexample does not affect the reward. Both runs conduct 40 training steps, and are evaluated at 10, 20, 30 and 40 steps. Their results on the common evaluation set after 40 steps are provided below (Figure 4; Appendix G.1, Table 23):
| Evaluation metric after 40 training steps | Verdict-only, original distribution | Verdict-only, balanced distribution | Full reward |
|---|---|---|---|
| Verdict Accuracy | 62.00% | 65.75% | 66.50% |
| Hack Success | 25.94% | 34.96% | 50.00% |
Class balancing mitigates the drop in the tool usage observed under the original distribution and increases Hack Success. However, while the balanced variant approaches the Verdict Accuracy of the full reward, its Hack Success still lags behind by 15.04 percentage points. For the task of making the acceptance decision and providing the failure evidence, optimizing only verdicts does not provide the same capability of counterexample discovery.
Q3: Length-penalty scheduling and sensitivity
We would like to clarify the criteria of scheduling, and the additional comparisons provided in Appendix C, Appendix G.4 and Figure 14. We address the criteria of scheduling, evaluation results and choice of ρ below.
1. What criterion and data determine whether to enable or disable the penalty? We monitor the raw task reward, response length, abort rate and interaction depth during training. When the level of the task reward plateaus while the response length continues to increase, we resume from a nearby checkpoint at a ten-step boundary with the penalty enabled. When the continuation of length reduction is accompanied by the decreasing interaction depth and task performance, we resume with the penalty disabled. The penalty is enabled during [90, 110), [160, 180), and [230, 250); otherwise, it is disabled. This schedule is chosen manually based on these observations.
Why disable the penalty after checkpoint 109 rather than keep it enabled? Appendix G.4 reports the evaluation results of the continuous ρ=75 branch: Verdict Accuracy drops from 79.75% at checkpoint 109 to 75.75% at checkpoint 119. This supports resuming with the penalty disabled from checkpoint 109.
2. How does enabling the penalty affect the final accuracy and abort rates? Starting from the same checkpoint 89, with the identical data and all other training parameters, we compare no length penalty with the phased ρ=75 schedule at checkpoint 179 (Table 27):
| Evaluation metric | No length penalty | ρ=75 |
|---|---|---|
| Verdict Accuracy | 78.00% | 82.25% |
| Hack Success | 61.28% | 64.29% |
| Aborted trajectories | 25.50% | 10.25% |
The phased schedule improves Verdict Accuracy by 4.25 percentage points and Hack Success by 3.01 percentage points, and reduces the abort rate by 15.25 percentage points. The accuracy here includes all 400 candidates, with aborted evaluation trajectories being assigned the Accepted prediction, consistent with Table 27 and Appendix G.4.
Appendix D.1 also reports an alternative scoring rule that counts every incomplete trajectory as incorrect. Under this rule, the accuracy without the penalty decreases from 74.8% at checkpoint 79 to 62.5% at checkpoint 179; the phased schedule achieves 74.5% at checkpoint 179. Both scoring rules demonstrate the benefit from the length control, comparing under their definitions. The trajectories that exceed the wall-clock budget are excluded from the policy update in all branches. The experiments above vary the length-penalty setting while keeping the rule common.
3. Why ρ=75 rather than ρ=50, and why not keep the penalty enabled throughout? The threshold is a percentile of the response length among the trajectories with the highest reward in each group and is recomputed at every step. With ρ=50, a stronger compression is enforced: approximately 47% of the successful trajectories get a penalty in the compared training windows, while it is approximately 25% with ρ=75. The continuous-penalty runs are reported in Table 28 below. The metrics are aggregated over the consecutive five-step windows; response length and interaction turns are averaged over per-step medians of each five-step window.
| ρ | Training steps | Response length (tokens) | Interaction turns | Abort rate | Hack Success | Verdict Accuracy |
|---|---|---|---|---|---|---|
| 50 | [105, 110) | 20,017 | 8.6 | 7.58% | 71.24% | 84.76% |
| 50 | [115, 120) | 15,277 | 7.0 | 2.36% | 69.98% | 84.65% |
| 75 | [105, 110) | 21,082 | 9.2 | 8.60% | 71.36% | 84.65% |
| 75 | [115, 120) | 17,274 | 8.4 | 5.43% | 72.26% | 85.11% |
| 75 | [120, 125) | 14,691 | 7.8 | 3.34% | 72.49% | 85.21% |
| 75 | [125, 130) | 12,736 | 7.2 | 2.10% | 70.57% | 85.34% |
| 75 | [130, 135) | 10,813 | 6.8 | 0.99% | 67.61% | 83.92% |
Across the common [105, 110)→[115, 120) windows, ρ=50 decreases the response length by 23.7%, interaction turns from 8.6 to 7.0, while lowering Hack Success by 1.26 percentage points. When ρ=75 is chosen, there is an 18.1% reduction in the response length, better preservation of interaction turns, and 0.90 percentage points increase in the Hack Success metric. It supports our decision to use the milder ρ=75 configuration.
However, when ρ=75 is always used, Hack Success begins to decline in [125, 130), followed by Verdict Accuracy in [130, 135), and response length becomes shorter, with the abort rate continuing to decrease. As a result, we alternate enabling and disabling the penalty to control the abort rate and preserve the ability to discover counterexamples.
Once again, thank you very much for your detailed comments and suggestions for the necessary comparisons in order to measure the contribution of our work. We will really appreciate your reconsideration of your assessment and score based on the above responses.
References
[1] Zeyao Ma et al. Scaling Agentic Verifier for Competitive Coding. 2026.
[2] Qingyao Li et al. ATGen: Adversarial Reinforcement Learning for Test Case Generation. 2025.
[3] Archiki Prasad, Elias Stengel-Eskin, Justin Chih-Yao Chen, Zaid Khan, and Mohit Bansal. Learning to Generate Unit Tests for Automated Debugging. 2025.
[4] Haichuan Hu, Xiaochen Xie, and Quanjun Zhang. Repair-R1: Better Test Before Repair. 2025.
We would like to thank the reviewer for acknowledging (i) the usefulness of USACO-JUDGE for making the acceptance decision and finding counterexamples, and (ii) the considerable improvement from training with the same backbone and agentic scaffold.
W1: Task and methodological contribution
We would like to note that the methodological contribution of this paper is in designing training for a verifier that makes the acceptance decision regarding the candidate program and provides the rationale and an executable counterexample in case of a suspicion of any failure other than a compilation one. GRPO optimization and execution capabilities are not claimed to be novel.
Distinction from previous test generation methods. Ma et al. [1] generate test inputs that distinguish between the behaviors of pairs of candidate programs and use them for execution-based voting. ATGen [2] employs adversarial training to improve test-output correctness and attack success. Our input is a problem statement and a single candidate program of unknown correctness. The verifier is supposed to make an acceptance decision, give a rationale for it and provide an executable counterexample in case of a rejection other than because of a compilation error. The latter task additionally requires making the decision and validating the evidence of rejecting the program. The differences are discussed in Section 2.
Reward for the whole judging task. The correct program does not have any valid counterexample; therefore, the correct acceptance should be rewarded as well. In case of rejections that require a counterexample, the main reward is in exposing the failure with the executable evidence. Successful generator execution and input validity serve as the checkable signs of progress for unsuccessful attempts. Section 4.2 incorporates the attempts into the single reward scheme for the verifier.
USACO-JUDGE consists of both correct and incorrect candidates, allowing evaluating the acceptance decision as well as the ability of finding counterexamples. With the framework of the same backbone and agentic scaffold, the training raises USACO-JUDGE Verdict Accuracy from 71.41% to 87.41% and overall Hack Success from 40.61% to 62.67%. The additional verdict-only and binary outcome-reward ablations of the training objective are conducted to investigate it further; the evidence will be discussed in our response to W3, W4, and Q2.
W2: Training of the feedback interface and evaluation of diagnosis quality
We would like to note that (V, D, X) defines the feedback interface of the verifier, and the training is based on agentic GRPO. The contribution of the paper is in training this capability with verifiable verdict and counterexample rewards. The three output fields are not presented as a new optimization algorithm.
Why D does not get a correctness reward. This is the deliberate design choice. It is possible to check if a valid input causes a failure of the program through execution. Evaluating the diagnosis to be correct, complete and helpful would require the capabilities of a reasoning-capable judge, which is costly for training. Therefore, the D is requested via the prompt, and the entire trajectory is optimized via reinforcement learning without a separate scorer of diagnosis correctness. The 0.05 penalty for D exceeding 1,000 tokens in Section 4.2 is applied only for length control. The quality and helpfulness of the diagnosis are evaluated via separate audits and feedback ablations.
Section 6.1, Figure 8 and Appendix F.6 (Table 21) compare the agentic base and ARBITER on the same 400 USACO-JUDGE candidates:
Three competitive programmers evaluated 1,200 diagnoses generated for these candidates. When partially correct diagnoses are not counted as correct, the denominator is all 400 candidates. The base is already agentic and prompted to provide an explanation, thus this comparison evaluates the gain in diagnosis quality from the training directly, not only in prompting the model to give an explanation.
Does the diagnosis help repair? Table 2 adds the V-only condition that maintains the same verifier, solver, starting programs, and selection protocol, but passes V only to the solver. Adding D improves all six combinations of solver and difficulty at @8 and five combinations at @1, with one tie. For example, GPT-OSS-120B improves from 79.2 to 89.2 on Medium at @8, and from 33.1 to 39.1 on Hard. This supports the additional benefit from D for repairing over the selection and stopping based on verdict alone.