acceptodds
Under review as a conference paper at ICLR 2027

LLM-as-a-Verifier: A General-Purpose Verification Framework

Abstract

Scaling pre-training, post-training, and test-time compute have become the central paradigms for improving the capabilities of large language models (LLMs). In this work, we identify verification—the ability to determine the correctness of a solution—as a new scaling axis. To unlock this, we introduce LLM-as-a-Verifier, a general-purpose verification framework that provides fine-grained feedback for agents without requiring additional training, and systematically characterize how verification scales. Specifically, we identify three orthogonal dimensions of verification scaling: (1) score granularity, (2) repeated evaluation, and (3) criteria decomposition, and show that they provide complementary gains and should be scaled in tandem to achieve optimal performance. In particular, we show for the first time that scaling score granularity improves the separation between correct and incorrect solutions, yielding better-calibrated comparisons than the conventional 1–5 scale. To make verification scaling practical, we propose Probabilistic Pivot Tournament, a compute-efficient ranking algorithm that mitigates positional bias and adaptively allocates verification compute toward stronger and uncertain candidates, reducing the number of pairwise comparisons from to . When used as a trajectory reward model for test-time scaling, LLM-as-a-Verifier achieves state-of-the-art performance on Terminal-Bench V2 (86.5%), SWE-Bench Verified (78.2%), RoboRewardBench (87.4%), and MedAgentBench (73.3%). We also find that pairing LLM-as-a-Verifier with an open-weight model outperforms closed-source frontier baselines on Terminal-Bench 2.1 with substantially lower cost. Beyond verification, the fine-grained signals from LLM-as-a-Verifier can also serve as a proxy for estimating task progress. We build an extension for Claude Code, enabling developers to monitor and improve their own agentic systems. Finally, we show that LLM-as-a-Verifier can be used as a dense reward signal for RL, improving the sample efficiency of SAC and GRPO on robotics and mathematical reasoning benchmarks. Interestingly, our approach also improves the effectiveness of RL in non-verifiable domains without ground-truth checkers, such as painting, substantially outperforming a standard LLM-as-a-Judge baseline.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Agent Verification, Reward Modeling, Alignment, Test-Time Scaling, Reinforcement Learning

Reviews

Among:
Shape:
1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_xVwXOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper presents LLM-as-a-Verifier, a training-free framework for evaluating agent trajectories. It combines probability-weighted scoring with finer score levels, repeated evaluation, and separate evaluation criteria. It also introduces a Probabilistic Pivot Tournament to reduce the number of candidate comparisons. Experiments cover coding, robotic trajectory evaluation, and medical tasks, with additional applications to progress monitoring and reinforcement learning. The central claim is that improving verification can help agents select better solutions and obtain more useful feedback.

Critical strengths

S1. The paper addresses a practical bottleneck: agents often generate successful trajectories but fail to select them reliably. Reporting both single-candidate performance and oracle selection performance makes this motivation concrete.

S2. The framework works with existing language and vision-language models without additional verifier training. Its application across coding, robotics, and medical tasks gives it practical relevance.

S3. The experiments examine several useful aspects of verification, including scoring granularity, repeated evaluation, ranking budgets, and caching. The extensions to progress monitoring and reinforcement learning broaden the potential applications.

Critical weaknesses

W1. Counting ties as errors in Appendix D overstates the selection benefit of continuous scoring. In Table 3, random tie-breaking would give the discrete baseline an expected accuracy of 80.35% with one evaluation, versus 80.1% for the continuous method. The main results also need an explicit tie-breaking rule.

W2. The three-criterion ensemble uses more verifier calls than the individual criteria. The key missing control is repeated evaluation with one criterion under the same total budget, which would separate the benefit of different criteria from that of additional evaluations.

W3. PPT needs a comparison with V1 using the same scorer, criteria, and total evaluation budget, plus a random-pivot baseline. Its pivot selection also relies on scores alone, despite the claim of uncertainty-aware allocation.

W4. VOC measures agreement with chronological order and can remain high when a trajectory stalls before completion. Progress tracking should be evaluated against intermediate completion labels and on trajectories with stalls, regressions, and failures.

Questions for authors

Q1. How are ties handled in Figures 3 and 8 and in final trajectory selection? How do the comparisons change when ties are resolved randomly?

Q2. Under the same total verification budget, how does the three-criterion ensemble compare with repeated evaluation using one criterion?

Q3. How does PPT compare with V1 and random-pivot selection when all methods use the same scorer, evaluation criteria, and repetition settings?

3 comments
AuthorsOpenReview ↗

Response to Reviewer xVwX (Part 1)

Dear Reviewer xVwX,

Thank you for your thoughtful review and constructive feedback. We have updated the paper in line with your comments. Changes are marked in green\color{green}{\textbf{green}} in the revised manuscript. Below, we address the comments in your review.

Concrete steps we took based on your feedback:

  • Stated the tie-handling protocol explicitly and clarified its description in Appendix D (Section 4, Appendices D and E, green coloring)\color{green}{\textbf{(Section 4, Appendices D and E, green coloring)}}
  • Reported the discrete judge's strict accuracy, tie rate, and accuracy under random tie-breaking side by side (Table 6, green coloring)\color{green}{\textbf{(Table 6, green coloring)}}
  • Compared the three-criterion ensemble against single criteria (Appendix Q, Table 16, green coloring)\color{green}{\textbf{(Appendix Q, Table 16, green coloring)}}
  • Added a random-pivot baseline and further PPT ablations (Appendix C.1, Tables 3 and 4, blue coloring)\color{blue}{\textbf{(Appendix C.1, Tables 3 and 4, blue coloring)}}
  • Computed VOC on failed trajectories and clarified the use of VOC (Section 6, green coloring)\color{green}{\textbf{(Section 6, green coloring)}}

W1 & Q1: Tie handling

Ties are assigned 0.5 credit throughout the paper, which is the expected accuracy under random tie-breaking:

Accuracy=P(sc>si)+12P(sc=si),\mathrm{Accuracy} = P(s_c > s_i) + \tfrac{1}{2}P(s_c = s_i),

where scs_c and sis_i are the scores of the correct and incorrect trajectories. This protocol already applies to Figures 3 and 8 and to the closed-model table in Appendix D (Table 3 in the original submission, Table 5 in the revision). The strict-preference description in the original text only applied to the continuous verifier, as in Figure 3: it produces zero ties, so strict accuracy and accuracy under random tie-breaking are identical. For the discrete baseline, the reported accuracies already include the half credit, so they should not be adjusted further. We have revised Appendix D to state this protocol explicitly.

Figure 3 is unchanged, since continuous scores produce no ties and strict accuracy equals accuracy under random tie-breaking. For Figure 8, we now additionally report the discrete judge under both protocols:

kStrict accuracy (ties incorrect)Tie rateAccuracy (random tie-breaking)
158.5%26.7%71.8%
468.6%11.7%74.4%
1672.0%5.5%74.7%

Random tie-breaking improves the discrete judge relative to counting ties as incorrect. Even so, the continuous verifier reaches 74.7% with a single evaluation, matching the discrete judge's 74.7% after 16 repeated evaluations. This demonstrates that continuous scoring provides comparable discrimination with substantially fewer evaluations.

W2 & Q2: Three-criterion ensemble vs. one criterion

Under 16 repeated evaluations, we obtain:

MethodAccuracy (mean ± SD)
Specification75.22 ± 2.13%
Error signals76.05 ± 1.71%
Output match76.38 ± 2.20%
Ensemble (all three, one combined prompt)74.34 ± 1.84%
Ensemble (all three, separate prompts)78.29 ± 1.43%

We find that a single criterion reaches at most 76.38%, while the ensemble over separate prompts reaches 78.29%. Placing all three criteria in one combined prompt reduces accuracy to 74.34%.

AuthorsOpenReview ↗

Response to Reviewer xVwX (Part 2)

W3 & Q3: PPT vs. V1 and random-pivot selection

Ring-based vs. random pivot selection. To isolate the effect of pivot selection, we evaluate ring-selected pivots against randomly chosen pivots on the existing 20-candidate pools (Terminus-2 harness, 89 tasks). All variants share the same verifier, evaluation criteria, repeated-evaluation settings, and number of pivot comparisons, so they differ only in how the five pivots are selected. Results are mean ± std over three seeds, each with a different random ring or set of random pivots. Ring-based selection is better than random selection on every seed, improving the success rate by 3 points.

MethodPairs queriedTB 2.0 success rate
Pass@1—52.64%
Ring pass only (no pivot rounds)1,06062.55 ± 1.72%
Random pivots (pivot rounds)5,55063.30 ± 2.83%
Ring-based pivots (PPT)5,55066.29 ± 1.95%

Quality of the selected pivots. We also examine the pivots themselves on the 70 swing tasks, whose pools contain both passing and failing trajectories. Ring-based selection raises the fraction of passing pivots by 14.3 points, so PPT spends its verification budget on candidates that are more likely to be correct.

MetricRandom pivotsRing-based pivots (PPT)
Fraction of pivots that are passing trajectories50.8 ± 0.9%65.1 ± 0.6%
Tasks with at least one passing pivot84.8 ± 2.2%91.0 ± 1.6%
Tasks where all 5 pivots pass14.8 ± 2.2%36.2 ± 0.8%
Tasks with no passing pivot (lower is better)15.2 ± 2.2%9.0 ± 1.6%

Comparison with V1 and the budget–accuracy trade-off. On the same pools, PPT with only k=3k{=}3 achieves 66.17% using 4,723 pairs, surpassing the best V1 result (65.85%) while using 32.5% fewer comparisons. Raising the number of pivots to k=9k{=}9 gives 67.13% using 9,630 pairs, close to full round-robin (67.42%) with 26.5% fewer comparisons.

MethodTotal pairs queriedAccuracy
V1 (5N budget)7,00065.85%
PPT (k=3)4,72366.17%
PPT (k=5)6,61066.29%
PPT (k=9)9,63067.13%
Full round-robin13,11167.42%

W4: VOC and progress tracking on failed trajectories

We agree that VOC measures agreement with chronological order, and that its absolute value does not certify task completion. We therefore do not use VOC as an absolute measure of progress. We use it only for relative comparison: to rank parallel trajectories on the same task against each other and to identify the runs whose progress has plateaued. To test whether VOC supports this relative use, we evaluated it on trajectories with stalls, regressions, and failures, using 500 paired successful and failed trajectories from the same Terminal-Bench V2 tasks.

Trajectory outcomeSpearman VOC (rank correlation)
Successful0.848 ± 0.012
Failed0.769 ± 0.016

LLM-as-a-Verifier achieves a Spearman VOC of 0.848 on successful trajectories, compared with 0.769 on failed trajectories from the same tasks, a gap of 0.08. On successful trajectories, the verifier score rises consistently as the agent advances, which gives a high rank correlation with step order. On failed trajectories, the score more often plateaus when the agent stalls and drops after erroneous actions, and these flat or decreasing segments lower the correlation. As you point out, the VOC of a failed trajectory can still be high in absolute terms (0.769), which is exactly why we do not threshold it. What matters for our use is the relative ordering: on the same task, runs that stall or regress receive a lower VOC than runs that keep progressing.

Progress-aware scheduling relies only on this relative comparison. A run is paused when its VOC stops improving and falls below that of the other parallel runs on the same task (Appendix K, Algorithm 2). On Terminal-Bench V2, pausing stalled trajectories with VOC improves reward per GPU-hour by 2.2×, compared with 1.2× for a matched-rate random-stopping baseline, which shows that the relative VOC signal identifies the runs that are worth pausing.

We hope these clarifications and additional results address your concerns, and we hope you will consider updating your score in light of these improvements.

Thank you for the clarifications and additional experiments. While some concerns remain, I will raise my rating to 3.

Reviewer_vENBOpenReview ↗
Rating
4
Confidence
4
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper scores candidate solutions by the expected value of an LLM's score-token probabilities and picks the best one with a pairwise pivot tournament. It reports state-of-the-art best-of-N results on coding, robotics and medical agent benchmarks, and uses the same scores as dense RL rewards.

Critical strengths
  1. The paper offers an interesting view that verification itself can be scaled, along score granularity, repeated evaluation and criteria decomposition.
  2. The method is simple and training-free, and the same recipe applies to text and video for selection, progress tracking and RL rewards.
  3. Extensive experiments report state-of-the-art results across coding, robotics and medical benchmarks.
Critical weaknesses
  1. The verifier outputs only a scalar score: it does not say where the error is or how to fix it, and its reasoning is never evaluated, so "fine-grained feedback" amounts to finer score resolution.
  2. The paper does not explore whether a single trained verifier could internalize the criteria, repeated evaluations and order debiasing, which would avoid the many C × K pairwise calls at inference.
  3. There are no controlled perturbation tests (e.g., injecting or fixing a single error while keeping everything else fixed), so the verifier may rely on surface cues.
  4. Progress evaluation computes VOC only on successful trajectories, never tests whether prefix scores predict final outcomes, and compares early stopping and scheduling with no matched-rate random-stopping baseline.
  5. RL gains are reported per training step only, without the verifier's compute and time overhead.
Questions for authors

See Weaknesses.

3 comments
AuthorsOpenReview ↗

Response to Reviewer vENB (Part 1)

Dear Reviewer vENB,

Thank you so much for your very positive and thoughtful review. We have updated the paper in line with your comments. Changes are marked in brown\color{#964B00}{\textbf{brown}} in the revised manuscript. Below, we address each weakness in your review.

Concrete steps we took based on your feedback:

  • Defined "fine-grained feedback" as finer score resolution, and clarified that LLM-as-a-Verifier can track task progress and indicate where errors occur along a trajectory (Section 3.2, Section 6, Appendix S, brown coloring)\color{#964B00}{\textbf{(Section 3.2, Section 6, Appendix S, brown coloring)}}
  • Added a controlled perturbation test on 100 Terminal-Bench trajectories (Appendix R, Table 17, brown coloring)\color{#964B00}{\textbf{(Appendix R, Table 17, brown coloring)}}
  • Computed VOC on failed trajectories and on the first 70% prefix of each trajectory (Section 6, Table 13, brown and green coloring)\color{#964B00}{\textbf{(Section 6, Table 13, brown and green coloring)}}
  • Added a matched-rate random-stopping baseline for progress-aware scheduling (Section 6, Appendix K, brown coloring)\color{#964B00}{\textbf{(Section 6, Appendix K, brown coloring)}}
  • Clarified that LLM-as-a-Verifier introduces minimal latency for RL, as all verifier calls can run in parallel (Sections 4 and 7, Appendix S, brown coloring)\color{#964B00}{\textbf{(Sections 4 and 7, Appendix S, brown coloring)}}
  • Added verifier distillation as future work (Appendix S, brown coloring)\color{#964B00}{\textbf{(Appendix S, brown coloring)}}

W1: The verifier outputs only a scalar score

We have revised the manuscript to make the distinction clear: "fine-grained feedback" refers to finer score resolution, not to natural-language error localization or corrective instructions. The continuous score can still indicate where along a trajectory progress stalls or errors occur. In Section 6 and Figure 4, the verifier score tracks intermediate progress and drops at erroneous actions such as an unnecessary package installation and a compilation failure. The framework does not generate corrective instructions, but these signals are useful for monitoring agent execution and for RL.

W2: A single trained verifier that internalizes the criteria, repetitions, and order debiasing

We agree that distilling the verification signals into a smaller trained verifier is a promising direction, and we now list it as future work (Appendix S). Our primary contribution here is to show that verification can be scaled systematically across models without any additional training. We plan to explore distillation as a follow-up to reduce cost.

W3: No controlled perturbation tests

We added a perturbation test (Appendix R). We inject a single localized edit into a correct trajectory and ask the verifier to compare the original against the edited copy, with everything else held fixed. On 100 correct trajectories from our binary verification set, we test three kinds of edit:

  • Silent error: one substantive mistake, such as a wrong install path or constant, with no failure message and unchanged length
  • Explicit failure: a late verification output edited to show a failing test or traceback
  • Benign warning: a harmless warning line added while the solution stays correct
ConditionOriginal scored higherScore margin (1–20 scale)
Silent error93%3.74
Explicit failure97%10.91
Benign warning (still correct)70%0.11

The verifier assigns higher scores to the original trajectories in 93% of silent-error cases and 97% of explicit-failure cases, with average score margins of 3.74 and 10.91 points respectively. In contrast, benign warnings produce a negligible average score margin of only 0.11 points. These results demonstrate that the verifier is sensitive to substantive errors while remaining largely robust to superficial warning cues.

AuthorsOpenReview ↗

Response to Reviewer vENB (Part 2)

W4: VOC only on successful trajectories; prefix scores; random-stopping baseline

We ran additional experiments on 500 paired successful and failed trajectories from the same Terminal-Bench V2 tasks.

Failed trajectories and partial trajectories. The verifier achieves a Spearman VOC of 0.848 on successful trajectories and 0.769 on failed ones: successful trajectories show more consistent increases in verifier score, while failed trajectories show more stagnation and regression. The gap narrows only slightly, from 0.079 to 0.069, when we use only the first 70% prefix of each trajectory, so partial trajectories already exhibit progress patterns that distinguish successful from failed executions before the final outcome is observed.

Trajectory outcomeFull trajectory VOCFirst 70% VOC
Successful0.8480.827
Failed0.7690.758
Success–failure gap0.0790.069

Matched-rate random stopping. We added a baseline that pauses runs at the same rate as our scheduler but selects them at random. On Terminal-Bench V2, this baseline improves reward per GPU-hour by 1.2×, whereas progress-aware scheduling guided by LLM-as-a-Verifier achieves 2.2×. Most of the gain therefore comes from the verifier's progress signal identifying which runs to pause, rather than from stopping runs early.

W5: RL gains are reported per training step only

The three scaling dimensions can be parallelized: all verifier calls are independent and can be evaluated concurrently. With sufficient parallel compute, the additional evaluations therefore do not increase wall-clock latency. Verification scaling does increase total inference compute. A central motivation of our work is that allocating additional compute to verification produces more informative reward signals and improves downstream performance. The revised manuscript states that RL gains are reported per training step, clarifies that the verifier adds minimal wall-clock latency because its calls run in parallel, and acknowledges the additional verifier compute as a trade-off (Section 7, Appendix S).

We hope these clarifications and additional results address your concerns.

Thank you for your response. I decide to maintain my positive rating for your great work.

Reviewer_5LB6OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes a training-free verifier that averages probability-weighted score tokens over repeated evaluations and decomposed criteria. It studies these three design dimensions, introduces a pivot-based tournament for ranking trajectories, and applies the resulting scores to candidate selection, progress estimation, and RL rewards. The central question is whether spending inference compute on more discriminative verification improves agent performance across domains.

Critical strengths
  1. The paper addresses an important practical problem and evaluates it on challenging tasks. Reliably selecting successful agent trajectories remains difficult even when candidate pools contain correct solutions.
  2. The empirical investigation of verifier design is useful. The paper studies score granularity, repeated evaluation, and criteria decomposition, and reports improvements in distinguishing successful from failed trajectories.
  3. PPT offers a potentially useful comparison schedule for reducing verification cost.
Critical weaknesses
  1. The methodological and empirical contributions are insufficiently distinguished from prior work. Probability-weighted scoring and repeated sampling already appear in G-Eval [1], while decomposing evaluation into finer criteria is central to FLASK [2]. Best-of-N selection is also established, and using an off-the-shelf LLM directly as an RL reward predates this work, for example in direct-RLAIF [3]. Although the paper acknowledges some of these precedents, its broad framing makes it difficult to identify precisely what new knowledge or capability is established beyond assembling and applying these techniques. The contribution would be clearer if the paper explicitly separated established components, PPT’s specific design, and its new empirical findings.
  2. PPT’s specific design choices are not sufficiently isolated. Table 2 provides a useful budget comparison, but does not establish whether ring-based selection of strong pivots is better than random pivots or another simple schedule with the same budget and scoring procedure. It also does not separate the contributions of the ring initialization, pivot choice, and soft preference aggregation. Without these controls, the benefit attributable to the proposed tournament design remains uncertain. The connection between PPT and the headline results is unclear.

[1] Liu et al. (2023) G-Eval: NLG Evaluation using GPT-4 with Better Human Alignment [2] Ye et al. (2023), Flask: Fine-grained language model evaluation based on alignment skill sets [3] Lee at al. (2023), RLAIF vs. RLHF: Scaling Reinforcement Learning from Human Feedback with AI Feedback

Questions for authors
  1. What is the principal contribution beyond established LLM evaluation techniques? Is the intended advance PPT, the joint scaling analysis, or the empirical effectiveness of the combined framework on agent trajectories? Please distinguish these explicitly and explain which findings could not reasonably be inferred from prior work.
  2. Can you isolate PPT’s pivot-selection mechanism? On the existing 20-candidate pools, how does ring-selected PPT compare with random-pivot selection and a simple budget-matched comparison schedule, using exactly the same verifier, criteria, and repetition settings? Please report variability across random rings or seeds and task-level confidence intervals. What is the measured accuracy–cost trade-off attributable specifically to PPT?
4 comments
AuthorsOpenReview ↗

Response to Reviewer 5LB6 (Part 1)

Dear Reviewer 5LB6,

Thank you for your thoughtful review and constructive feedback. We have updated the paper in line with your comments. Changes are marked in blue\color{blue}{\textbf{blue}} in the revised manuscript. Below, we address the comments in your review.

Concrete steps we took based on your feedback:

  • Separated established components from our new findings in the Introduction and Related Work
  • Added an ablation of ring-based vs. random pivot selection at an identical budget, with three seeds (Appendix C.1, Table 3, blue coloring)\color{blue}{\text{(Appendix C.1, Table 3, blue coloring)}}
  • Added an analysis of the quality of the selected pivots (Table 4, blue coloring)\color{blue}{\text{(Table 4, blue coloring)}}
  • Added an ablation of Bradley–Terry aggregation vs. raw verifier scores (Appendix C.1, blue coloring)\color{blue}{\text{(Appendix C.1, blue coloring)}}
  • Stated the comparison savings of PPT against V1 and full round-robin explicitly (Appendix C, Table 2, blue coloring)\color{blue}{\text{(Appendix C, Table 2, blue coloring)}}

W1 & Q1: The contributions are insufficiently distinguished from prior work

Our main contributions are the following three, none of which can be inferred from prior work.

1) Score granularity as a scaling dimension. To our knowledge, we are the first to identify score granularity as a distinct scaling dimension for verification, and we provide both theoretical and empirical insights into its effectiveness. Standard practice holds that coarse scales (binary, ternary, or 1–5 Likert) work best [1, 2], and this is the common practitioner recommendation [3]. Empirically, we provide the first systematic evidence to the contrary: increasing granularity from 1–5 to 1–20 substantially improves verification and yields the largest gain of the three dimensions, with pairwise accuracy on Terminal-Bench improving from 73.1% at G=1G{=}1 to 77.5% at G=20G{=}20. Theoretically, Section 4.1 explains this through a signal-to-noise ratio (SNR) analysis that decomposes the score gap between correct and incorrect trajectories into signal strength and variance, and shows that pairwise accuracy is a monotonic function of the SNR. Consistent with this analysis, the measured SNR increases monotonically from 0.775 at G=1G{=}1 to 0.799 at G=20G{=}20. Appendix F gives a concrete example.

2) A systematic characterization of how verification scales. Our work is the first to systematically characterize the scaling behavior of LLM-based verification and to demonstrate that verification quality can be improved along multiple orthogonal dimensions. Analogous to the scaling laws introduced by Kaplan et al. [4], where data, model size, and compute must be scaled jointly to achieve optimal performance, our results show that score granularity, repeated evaluation, and criteria decomposition provide complementary gains and should likewise be scaled together. Crucially, by exposing and varying these dimensions independently, our study also quantifies the marginal contribution of each dimension relative to the others.

3) Probabilistic Pivot Tournament (PPT). PPT is an important algorithmic contribution of our work: it mitigates positional bias and adaptively allocates verification compute toward stronger and more uncertain candidates. As shown in Table 2, PPT outperforms the strongest existing ranking baseline, V1, introduced by Singh et al. [5]. Section 3.2 and Algorithm 1 provide the complete algorithmic details, including how we mitigate positional bias, derive preference probabilities, and allocate the verification budget. Appendix C further characterizes the budget–accuracy trade-off of PPT and shows that performance improves consistently as the number of pivots increases. We also provide additional ablations below that isolate the contribution of each of PPT's design choices.

For a detailed comparison with prior work, we kindly refer the reviewer to the updated Introduction section and Appendix M.


[1] Huang et al. "ChatGPT Rates Natural Language Explanation Quality like Humans: But on Which Scales?" arXiv preprint arXiv:2403.17368 (2024).

[2] Li et al. "Grading Scale Impact on LLM-as-a-Judge: Human-LLM Alignment Is Highest on 0-5 Grading Scale." arXiv preprint arXiv:2601.03444 (2026).

[3] LangChain. "Evaluating AI Agents at the Run, Trace, and Thread Level." LangChain, June 23, 2026.

[4] Kaplan et al. "Scaling Laws for Neural Language Models." arXiv preprint arXiv:2001.08361 (2020).

[5] Singh et al. "V₁: Unifying Generation and Self-Verification for Parallel Reasoners." arXiv preprint arXiv:2603.04304 (2026).

AuthorsOpenReview ↗

Response to Reviewer 5LB6 (Part 2)

W2 & Q2: Isolating PPT's design choices

Ring-based vs. random pivots. We compare ring-selected pivots against randomly selected pivots on the existing 20-candidate pools (Terminus-2 harness, 89 tasks). The verifier, evaluation criteria, repeated-evaluation settings, and number of pivot comparisons are fixed, so the only difference is how the five pivots are chosen. We report mean ± std over three seeds, with a different random ring or set of random pivots per seed. Ring-based selection outperforms random selection on all three seeds, by 3 points.

MethodPairs queriedTB 2.0 success rate
Pass@1—52.64%
Ring pass only (no pivot rounds)1,06062.55 ± 1.72%
Random pivots (pivot rounds)5,55063.30 ± 2.83%
Ring-based pivots (PPT)5,55066.29 ± 1.95%

Quality of the selected pivots. On the 70 swing tasks whose pool contains both passing and failing trajectories, ring-based selection increases the fraction of passing pivots by 14.3 points. PPT therefore concentrates its budget on candidates that are more likely to be correct.

MetricRandom pivotsRing-based pivots (PPT)
Fraction of pivots that are passing trajectories50.8 ± 0.9%65.1 ± 0.6%
Tasks with at least one passing pivot84.8 ± 2.2%91.0 ± 1.6%
Tasks where all 5 pivots pass14.8 ± 2.2%36.2 ± 0.8%
Tasks with no passing pivot (lower is better)15.2 ± 2.2%9.0 ± 1.6%

Soft preference aggregation. Bradley–Terry aggregation achieves 66.29 ± 1.95%, compared with 64.42 ± 1.30% when raw verifier scores on the 1–20 scale are used directly.

Accuracy–cost trade-off. On the same pools, PPT with k=3k{=}3 reaches 66.17% with 4,723 pairs, outperforming the best V1 result (65.85%) with 32.5% fewer comparisons. With k=9k{=}9 it reaches 67.13% with 9,630 pairs, approaching full round-robin (67.42%) with 26.5% fewer comparisons.

MethodTotal pairs queriedAccuracy
V1 (5N budget)7,00065.85%
PPT (k=3)4,72366.17%
PPT (k=5)6,61066.29%
PPT (k=9)9,63067.13%
Full round-robin13,11167.42%

We hope these clarifications and additional results address your concerns, and we hope you will consider updating your score in light of these improvements.

Thank you again for your time and thoughtful feedback! We hope our responses have addressed your concerns, and we are happy to provide any additional clarifications.

Thank you for the clarifications and additional ablations. I see the strongest potential contribution as demonstrating that a simple, training-free scoring configuration can improve verification and downstream agent performance at a favorable computational cost.

My remaining concern is (1) whether the scaling analysis provides sufficiently actionable insight beyond the observed improvements. The reported gains appear modest, and repeated evaluation exhibits diminishing returns, as the paper acknowledges. Although the paper draws an analogy to established scaling laws, it does not provide a predictive relationship indicating how performance should change as these dimensions increase, where gains saturate, or when further scaling is worthwhile.

More importantly, (2) increasing repetitions and evaluation criteria introduces additional computational cost. I appreciate the analyses of PPT, caching, and overall cost–quality trade-offs, but it remains unclear how practitioners should allocate a fixed budget across the available choices. For example, when should they spend additional compute on more repetitions, more criteria, or more candidate trajectories? A budget-matched comparison of configurations, together with practical recommendations, would make the empirical contribution more compelling.

Nevertheless, I appreciate the paper’s comprehensive empirical analysis and its potential value to the community, and I am therefore raising my score to a positive assessment.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Loading the map…

Discussion (0)

Sign in to comment.