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Under review as a conference paper at ICLR 2027

The Hidden Signal of Verifier Strictness: Controlling and Improving Step-Wise Verification via Selective Latent Steering

Abstract

Generative verifiers have emerged as a promising paradigm for step-wise verification, but their verification behavior is often poorly calibrated: they may be under-critical and miss erroneous steps, or over-critical and reject correct reasoning. We refer to the verifier's tendency toward stricter or more lenient judgments as verifier strictness. We identify hidden-state directions at verification-paragraph boundaries that modulate verifier strictness without fine-tuning the verifier. However, uniform steering induces a trade-off between error detection and correctness certification. To address this, we propose VerifySteer, which exploits latent correctness signals for sample-level routing and selectively intervenes on paragraph boundaries. Experiments on ProcessBench and Hard2Verify show that VerifySteer outperforms prompt optimization and activation steering baselines, and is competitive with self-consistency while requiring - less inference compute. VerifySteer is also complementary to verification fine-tuning, providing further gains on top of fine-tuned verifiers.

Primary area:
foundation or frontier models, including LLMs
Keywords:
generative verification, large language model

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_vgCFOpenReview ↗
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Paper summary

This paper studies the strictness of generative step-wise verifiers: overly lenient verifiers accept incorrect reasoning, whereas overly critical verifiers reject valid solutions. The authors construct activation directions from contrasting verification outcomes and introduce VerifySteer, which combines a correctness probe for sample-level routing with selective intervention at paragraph boundaries. Experiments on ProcessBench and Hard2Verify show improvements across model sizes, thinking modes, and a fine-tuned verifier. The method offers a promising performance–compute trade-off relative to self-consistency. The main unresolved issues concern data independence, the interpretation of the steering directions, and whether the selective gate identifies informative intervention locations beyond simply reducing perturbations.

Critical strengths
  1. Clear motivation and targeted design. The paper identifies the trade-off induced by uniformly increasing verifier strictness and proposes two complementary forms of adaptivity to address it.
  2. Consistent empirical improvements across settings. VerifySteer improves over optimized prompts on both benchmarks. The improvement on FARE-20B—from 41.5 to 51.1 F1—is particularly encouraging because it demonstrates compatibility with verification fine-tuning.
  3. Useful component ablations. The probe-only baseline, removal of each adaptive component, and comparison with adjacent content-token steering help establish that the results are not explained solely by the correctness probe or an arbitrary intervention site.
  4. Promising inference efficiency with development costs acknowledged. The method achieves performance competitive with multi-sample self-consistency at substantially lower estimated inference FLOPs. Reporting vector-construction costs and an amortization example improves the transparency of this comparison.
Critical weaknesses
  1. Data independence and the units of the development splits need clarification. Appendices D.2–D.4 describe several ActPRM-derived pools for vector construction, probe training, and model selection, but their relationships are not fully clear. In particular, the Hard2Verify setup describes 812 competition problems for vector construction and 2,448 training plus 1,050 validation samples for the probe. These counts may refer to different pools or multiple solutions per problem, but this should be explicit.

  2. The evidence supports behavioral control more strongly than a verification-specific strictness representation. Contrasting true rejection with false acceptance on the same problem–solution pair is a useful design. Nevertheless, the resulting direction may encode generic rejection behavior, successful mathematical checking, or differences in preceding verification trajectories. The current results do not fully distinguish these possibilities.

  3. The contribution to error localization should be separated from the change in acceptance behavior. TNR requires the correct first-error index, so its improvement is meaningful. However, it combines detecting that a solution is incorrect with localizing the first error. The reported aggregate does not show how much each component improves.

Questions for authors
  1. Can you provide a unified accounting of the development pools, including their numbers of unique problems, candidate solutions, and rollouts? Are all relevant splits problem-disjoint, and were benchmark overlaps explicitly removed?
  2. How do the steering directions compare with generic accept/reject directions? Can a shared vector transfer across ProcessBench subsets or to Hard2Verify without domain-specific reconstruction?
  3. Can you decompose the improvements into incorrect-solution detection and first-error localization, including conditional localization accuracy and error-transition counts?
  4. Does the cosine-based gate outperform a random gate matched for the number of interventions per sample?
  5. Can you report paired uncertainty estimates and sensitivity to vector-construction and probe-training seeds, particularly for comparisons with self-consistency?
2 comments
AuthorsOpenReview ↗

Authors' Response to Reviewer vgCF (Part 1)

We thank the reviewer for their thoughtful review and are glad that you found our work "clear motivation and targeted design", "useful component ablations" and "promising inference efficiency". We address each comment below.

W1. Data independence and the units of the development splits need clarification. Appendices D.2–D.4 describe several ActPRM-derived pools for vector construction, probe training, and model selection, but their relationships are not fully clear. In particular, the Hard2Verify setup describes 812 competition problems for vector construction and 2,448 training plus 1,050 validation samples for the probe. These counts may refer to different pools or multiple solutions per problem, but this should be explicit.

Q1. Can you provide a unified accounting of the development pools, including their numbers of unique problems, candidate solutions, and rollouts? Are all relevant splits problem-disjoint, and were benchmark overlaps explicitly removed?

We provide a unified accounting of development pools below and clarify the units and relationships. We have added these details to Appendix D.2.

All pools are drawn from ActPRM [1], where each item is one (problem, solution) pair with step-level labels. All counts in Appendix D are pairs. We sample pairs as given by ActPRM, without filtering by problem, following prior use of this dataset [1-2]. Therefore, we did not track the number of unique problems separately.

For vector construction, the verifier generates 16 verification traces per pair. The probe uses no rollouts.

No overlap with test benchmarks. ActPRM is reported to be decontaminated against ProcessBench [1], so no pool overlaps with ProcessBench test problems. We further checked our sampled pools against the Hard2Verify benchmark with fuzzy matching, and found no overlapping problems.

Train and validation sets are disjoint. Within each component (probe and layer selection), the train and validation sets are sampled to be disjoint.

Pools for different components are not enforced to be problem-disjoint, but this does not affect the validity of the evaluation. We sample each pool (for the vector, probe, and hyperparameters) at the level of pairs. All pools are used only for method development, and all reported results are evaluated on the test benchmarks. In addition, each pool is a small draw from ActPRM, with at most 8.5K pairs per pool out of the 663K pairs in the full dataset, so overlap between pools is small. For Hard2Verify, the vector pool (812 pairs) and the probe data (3,498 pairs) are drawn separately from ActPRM.

Table 9. Summary of development pools drawn from ActPRM.

Pool# (Problem, Solution) PairsVerifier rollouts per pair
GSM8K vector1,00016
MATH vector4,22416
OlympiadBench / Omni-MATH vector5,13216
Hard2Verify vector81216
Probe, ProcessBench8,500 (6,190 train + 2,310 val)-
Probe, Hard2Verify3,498 (2,448 train + 1,050 val)-
Hyperparameters, Layer selection1,00016

Reference

[1] Duan et al. Efficient Process Reward Model Training via Active Learning

[2] Xu et al. Foundational Automatic Evaluators: Scaling Multi-Task Generative Evaluator Training for Reasoning-Centric Domains

 


 

W2. The evidence supports behavioral control more strongly than a verification-specific strictness representation. Contrasting true rejection with false acceptance on the same problem–solution pair is a useful design. Nevertheless, the resulting direction may encode generic rejection behavior, successful mathematical checking, or differences in preceding verification trajectories. The current results do not fully distinguish these possibilities.

We agree with the reviewer that our evidence supports behavioral control, and in fact this is the main claim of our submission: behavioral control of verifier strictness through a hidden-state signal. Our writing is framed around this. For example, in Section 1, we begin by defining strictness as a behavioral dimension. In Contribution 1, we state that we identify a hidden-state signal associated with this behavioral dimension. The abstract describes "hidden-state directions at verification-paragraph boundaries that modulate verifier strictness".

The steering vector may indeed combine the behaviors the reviewer lists. Our case studies in Tables 1 and 6 show this qualitatively: after steering, the verifier both rejects the step and re-checks the math, recomputing the expression and stating the correct value. Our work discovers a steering direction beneficial to verification, and we show that it improves TNR, TPR, and F1 on verification benchmarks. Disentangling generic rejection, mathematical checking, and trajectory effects into separate steering vectors for finer-grained control is an interesting direction for future work.

AuthorsOpenReview ↗

Authors' Response to Reviewer vgCF (Part 2)

Q2. Can a shared vector transfer across ProcessBench subsets or to Hard2Verify without domain-specific reconstruction?

Our current setup already tests steering vector generalization across subsets, and we add new results on transfer between two subsets.

  • The GSM8K steering vector is built from a random 1K ActPRM subset.
  • OlympiadBench and Omni-MATH share a single vector, built from a random 5K-pair subset of the "olympiads" source label, a broad category that covers about 197K samples from diverse contests.

With this setup, VerifySteer improves over baselines on all subsets, which demonstrates generalization.

New result. To further test generalization, we apply the GSM8K vector, built from a random ActPRM subset, to Omni-MATH, the hardest subset. On GSM8K, this vector improves F1 over prompt optimization by 6.4 in Table 2 of paper. In the table below, on Omni-MATH, it improves F1 over baseline by 3.7, matching the 3.5 by original vector from "olympiads" subset. Therefore, a vector built from random data that improves the easiest subset also improves olympiad-level verification. The experimental setup is Qwen3-1.7B on Omni-MATH.

Table 5. Transfer of the GSM8K (easy) steering vector to Omni-MATH (hard). Qwen3-8B on Omni-MATH split of ProcessBench.

MethodTNRTPRF1
Basic Prompt8.082.614.7
Prompt Optimization10.457.317.6
VerifySteer-Uni12.659.320.9 (+3.3)
VerifySteer-Uni w/ GSM8K vector12.458.920.5 (+2.9)
VerifySteer-Bi12.664.321.1 (+3.5)
VerifySteer-Bi w/ GSM8K vector12.961.421.3 (+3.7)

 


 

W3. The contribution to error localization should be separated from the change in acceptance behavior. TNR requires the correct first-error index, so its improvement is meaningful. However, it combines detecting that a solution is incorrect with localizing the first error. The reported aggregate does not show how much each component improves.

Q3. Can you decompose the improvements into incorrect-solution detection and first-error localization, including conditional localization accuracy and error-transition counts?

We thank the reviewer for this suggestion. We report new results below using the suggested metrics. Detection is the fraction of incorrect solutions that the verifier rejects. Conditional localization accuracy is the fraction of rejected incorrect solutions for which the verifier predicts the exact first error step. We also report the counts of each mistake type defined in Section 3: under-critical (accepting an incorrect solution), over-critical (rejecting a correct solution), and inaccurate step identification (rejecting at the wrong step).

We find that most of the gain of VerifySteer comes from more accurate localization. Conditional localization improves by 2.5, with 46 fewer inaccurate step identifications. This is larger than the gain in detection (+0.6) and the drop in under-critical mistakes (-13).

Table: Qwen3-8B on ProcessBench. TNR, TPR, and F1 are averaged over the four subsets. Detection, conditional localization, and mistake counts are pooled over the four subsets. Changes relative to prompt optimization in parentheses.

MethodTNR (↑)TPR (↑)F1 (↑)Detection (↑)Cond. localization (↑)# Under-critical (↓)# Inaccurate step (↓)# Over-critical (↓)
Prompt Optimization60.683.269.990.267.3209655204
VerifySteer-Uni63.283.171.790.7 (+0.5)69.6 (+2.3)196 (−13)612 (−43)203 (−1)
VerifySteer-Bi63.783.772.390.8 (+0.6)69.8 (+2.5)196 (−13)609 (−46)195 (−9)
Reviewer_nxjwOpenReview ↗
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Paper summary

This work investigates how to steer LLM verifiers' hidden states to control the strictness of the verifiers' outputs and proposes VerifySteer. Specifically, it suggests that the hidden states for verification step boundaries can be steered, which leads to changing the tendency of the verifier to accept or reject inputs. The authors define the steering vectors by comparing true rejections and false acceptances and also comparing true acceptances and false rejections, which is based on contrastive activation addition (CAA). To apply such steering adaptively for samples, it uses a trained MLP whose input is the hidden state to decide steering based on correctness scoring. Also, for each delimiter, it checks the delimiter's hidden state's alignment with the steering vector to determine delimiter-level steering. This work's empirical evaluation is performed on ProcessBench and Hard2Verify, suggesting that VerifySteer can improve the performance metrics in general.

Critical strengths
  • Determining the appropriate hidden states of verifiers for steering and empirically demonstrating that verification steering is possible can be meaningful contributions.
Critical weaknesses
  • I think this work needs to provide stronger empirical evidence to support VerifySteer's generalization (and thus the claims by this work). For instance, the authors state "We construct validation sets from ActPRM for both steering vector extraction and correctness probe training. ActPRM is built on problems from NuminaMath-1.5 (LI et al., 2024), which provides source labels for each problem. We exploit these labels to sample subsets that are aligned with ProcessBench subsets in terms of problem difficulty and type, using fuzzy matching on problem text to identify source-aligned examples." (L965). While I appreciate the information disclosure, overall, it appears to me that the steering vector construction and correctness probe training (and validation) are designed to be aligned with the benchmarks. In other words, the presented empirical results may suggest that the verifier can be steered toward acceptance or rejection using the proposed approach and a positive net gain can be obtained by adjusting the bias in the verifier for the benchmark(s), but still, this may not be about fixing under-critical and over-critical behaviors in general. And, presenting qualitative examples does not seem to be enough to support generalization.
  • Also, the approach involves training (the correctness probe) on benchmark-aligned/relevant data, where the correctness probe is a type of supervised verifier that the proposed pipeline leverages. This may suggest that the hidden states alone may not be a sufficient source of information to improve the verifier regarding its strictness.
Questions for authors

Please refer to the Critical Weaknesses section.

3 comments
AuthorsOpenReview ↗

Authors' Response to Reviewer nxjw (Part 1)

W1 Part1 I think this work needs to provide stronger empirical evidence to support VerifySteer's generalization (and thus the claims by this work). For instance, the authors state "We construct validation sets from ActPRM for both steering vector extraction and correctness probe training. ActPRM is built on problems from NuminaMath-1.5 (LI et al., 2024), which provides source labels for each problem. We exploit these labels to sample subsets that are aligned with ProcessBench subsets in terms of problem difficulty and type, using fuzzy matching on problem text to identify source-aligned examples." (L965). While I appreciate the information disclosure, overall, it appears to me that the steering vector construction and correctness probe training (and validation) are designed to be aligned with the benchmarks.

We respectfully disagree that our setup is designed to align with the benchmarks. Our current setup does not overfit on a per-split basis, as we apply one probe across multiple benchmark splits and one steering vector improves multiple splits. We show in new experiments that the vector built from random data, which improves grade-school-level GSM8K, also transfers to olympiad-level Omni-MATH. It matches the performance of the steering vector built from olympiad-level data.

All data for the steering vectors and the probe comes from ActPRM [1], a PRM training set built on NuminaMath-1.5 and decontaminated against ProcessBench. The existing components already generalize:

  • The correctness probe is trained on a random ActPRM subset. A single probe serves all four ProcessBench subsets, and generalizes across difficulty levels.
  • GSM8K steering vector is built from a random 1K-problem ActPRM subset.
  • Shared vector for OlympiadBench and Omni-MATH: a single steering vector, built from a random 5K-problem subset of the "olympiads" source label of ActPRM, which covers about 197K problems from diverse contests. This is a coarse choice, not benchmark targeting, and the same vector serves both subsets.

With this setup, the consistent improvement of VerifySteer over all four subsets demonstrates generalization.

New result. To further test generalization, we apply the GSM8K vector, built from a random ActPRM subset, to Omni-MATH, the hardest subset. On GSM8K, this vector improves F1 over prompt optimization by 6.4 in Table 2 of the paper. In the table below, on Omni-MATH, it improves F1 over baseline by 3.7, matching the 3.5 gain of the original vector from "olympiads" subset. Therefore, a vector built from random data that improves the easiest subset also improves olympiad-level verification. This suggests our method captures more general verifier strictness rather than features of a specific problem distribution. The experimental setup is Qwen3-1.7B on Omni-MATH.

Table 5. Transfer of the GSM8K (easy) steering vector to Omni-MATH (hard). Qwen3-8B on Omni-MATH split of ProcessBench.

MethodTNRTPRF1
Basic Prompt8.082.614.7
Prompt Optimization10.457.317.6
VerifySteer-Uni12.659.320.9 (+3.3)
VerifySteer-Uni w/ GSM8K vector12.458.920.5 (+2.9)
VerifySteer-Bi12.664.321.1 (+3.5)
VerifySteer-Bi w/ GSM8K vector12.961.421.3 (+3.7)

Reference

[1] Duan et al. Efficient Process Reward Model Training via Active Learning

AuthorsOpenReview ↗

Authors' Response to Reviewer nxjw (Part 2)

W1 Part2 In other words, the presented empirical results may suggest that the verifier can be steered toward acceptance or rejection using the proposed approach and a positive net gain can be obtained by adjusting the bias in the verifier for the benchmark(s), but still, this may not be about fixing under-critical and over-critical behaviors in general. And, presenting qualitative examples does not seem to be enough to support generalization.

We respectfully disagree and clarify that VerifySteer is not a global bias shift. A bias shift is in fact one of our baselines: uniform contrastive steering (CAA) [1]. Section 4.2 and Figure 2 show that this leads to a trade-off between TNR and TPR. VerifySteer is designed to avoid this bias shift.

To go beyond qualitative examples, we extend the comparison with CAA by breaking down mistake types, as defined in Section 3: under-critical (accepting an incorrect solution), over-critical (rejecting a correct solution), and inaccurate step identification (rejecting at the wrong step). As background, TNR increases only if the verifier predicts the exact first erroneous step. So adjusting the verifier bias toward rejection cannot solve step-level verification. For example, it may simply reject the first step it checks.

  • VerifySteer is not a bias shift. It improves TNR without lowering TPR. In contrast, a bias shift method raises TNR at the cost of TPR.
  • VerifySteer reduces all three types of mistakes, and especially reduces inaccurate step identification. In contrast, a bias shift reduces under-critical mistakes but adds 64 over-critical and 17 wrong-step mistakes.
  • We use one probe for all benchmark subsets. The probe predicts which vector to use once per sample, not per step. So the probe alone cannot improve step identification.

Table. Qwen3-8B on ProcessBench. Left three cols: metrics (TNR, TPR, F1), right three cols: counts of mistake types.

MethodTNR (↑)TPR (↑)F1 (↑)# Under-critical (↓)# Inaccurate Step Identification (↓)# Over-critical (↓)
Prompt Optimization60.683.269.9209655204
Bias Shift (CAA)61.977.968.8166 (-43)672 (+17)268 (+64)
VerifySteer-Uni63.283.171.7196 (-13)612 (-43)203 (-1)
VerifySteer-Bi63.783.772.3196 (-13)609 (-46)195 (-9)

Reference

[1] Rimsky et al. Steering llama 2 via contrastive activation addition.

AuthorsOpenReview ↗

Authors' Response to Reviewer nxjw (Part 3)

W2. Also, the approach involves training (the correctness probe) on benchmark-aligned/relevant data, where the correctness probe is a type of supervised verifier that the proposed pipeline leverages. This may suggest that the hidden states alone may not be a sufficient source of information to improve the verifier regarding its strictness.

First, the correctness probe is not trained on benchmark-aligned data. It is trained on one randomly sampled subset of ActPRM [1], a PRM training set decontaminated against ProcessBench. A single probe serves all four ProcessBench subsets and generalizes across difficulty levels.

Second, the probe alone gives little or no gain. To separate the contribution of the probe from the full method, the submission already includes a Probe-only baseline in Tables 2 and 3. It keeps the probe but removes steering: if the predicted score is below the threshold (the solution is likely incorrect), it returns the output of the prompt optimization verifier. Otherwise, it labels the solution as fully correct. The Probe-only baseline performs similarly to prompt optimization and underperforms VerifySteer-Bi by 3.3 to 4.3 F1.

Table: Overall F1 on ProcessBench, averaged over the four subsets.

MethodQwen3-1.7BQwen3-8B
Basic Prompt20.965.9
Prompt Opt.25.169.9
Probe-only25.469.0
VerifySteer-Bi29.772.3

Third, the probe’s input is the verifier’s own hidden states over the tokens of the problem and solution. So all information used by VerifySteer comes from the verifier’s hidden states. We only train a lightweight readout (a 3-layer MLP) of the correctness signal already present in them.

Such lightweight probes are a common way to read out information from LLM hidden states, rather than a separate supervised verifier. Prior work uses them to read out signals such as truthfulness [2], or harmfulness [3-4], where the latter serves as auxiliary information to guide steering. Similarly, our probe only provides a coarse correctness signal to choose between the strictness-increasing and leniency-increasing vectors. The steered LLM verifier remains responsible for checking each step, and for either locating the first error or accepting a correct solution.

Reference

[1] Duan et al. Efficient Process Reward Model Training via Active Learning. COLM 2025

[2] Marks and Tegmark. The Geometry of Truth: Emergent Linear Structure in Large Language Model Representations of True/False Datasets. COLM 2024.

[3] Lee et al. Programming Refusal with Conditional Activation Steering. ICLR 2025.

[4] Han et al. SafeSwitch: Steering Unsafe LLM Behavior via Internal Activation Signals. EMNLP Findings 2025.

Reviewer_wzhHOpenReview ↗
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Paper summary

In this paper, the authors study why LLM verifiers misjudge solution steps, either accepting wrong steps or rejecting correct ones, a tendency they call verifier strictness. They show that the verifier’s tendency to accept or reject a step is reflected in the hidden state of the paragraph break (“\n\n”) before each verification paragraph. Adding a steering vector at that position shifts the verifier toward stricter or more lenient judgments. They propose VerifySteer, which uses a small probe to predict whether a solution is correct, steers toward strictness or leniency accordingly, and steers only the paragraph breaks not already aligned with the chosen direction. On ProcessBench, VerifySteer improves F1 over prompt optimization by 4.6 points on Qwen3-1.7B and 2.4 points on Qwen3-8B. It is also competitive with self-consistency at 3 to 8× less inference compute.

Critical strengths
  1. Prior work has shown that LLM verifiers tend to accept flawed solutions, especially when the verifier is weaker than the generator [1, 2]. Fixing this usually requires fine-tuning on large step-labeled datasets. The authors show that verifier behaviour can instead be adjusted at inference time, without changing model weights, by steering hidden states at paragraph breaks in the verification trace. This gives a lightweight way to adapt verifiers as generator models change, without retraining them.

  2. The gains hold on top of fine-tuned verifiers and at low inference cost. Applying VerifySteer to FARE-20B raises Hard2Verify F1 from 41.5 to 51.1. Whereas, self-consistency with 8 samples reaches only 42.7, at about 6× the inference compute (Table 3). The steered Qwen3-8B also outperforms the prompt-optimized Qwen3-14B on both benchmarks.

[1] Pandit et al., Hard2Verify: A Step-Level Verification Benchmark for Open-Ended Frontier Math, 2025. [2] Lu et al., When Does Verification Pay Off? A Closer Look at LLMs as Solution Verifiers, 2025.

Critical weaknesses
  1. The authors motivate VerifySteer as a lightweight alternative to fine-tuning, which needs expensive step-level labels. However, VerifySteer also needs step-labeled data. Its steering vectors and probe are built from ActPRM, sampled to match each test benchmark’s difficulty and source.

  2. The authors claim that the verifiers accept-or-reject tendency is encoded in the hidden state of the “\n\n” token, and that steering it also corrects the verifier’s reasoning. However, steering the first content token after the break gives similar gains, e.g., 76.0 vs. 76.4 F1 on MATH for Qwen3-8B (Table 4). So it is not clear whether the signal is specific to the paragraph break or is spread across nearby tokens.

Questions for authors

Questions:

  1. Just curious, how does steering at the “\n\n” token compare with steering at randomly chosen tokens or at all generated tokens?

Typos:

  1. L301: greedy decoding.Table 1 (space is missing)
  2. L373: "Our method keeps the verifier frozen. The verifier stays frozen throughout" -- repeats the same point
1 comment
AuthorsOpenReview ↗

Authors' Response to Reviewer wzhH

W1 The authors motivate VerifySteer as a lightweight alternative to fine-tuning, which needs expensive step-level labels. However, VerifySteer also needs step-labeled data. Its steering vectors and probe are built from ActPRM, sampled to match each test benchmark’s difficulty and source.

This is a fair point. VerifySteer does need labeled data, but far less than fine-tuning. We use about 24K labeled pairs from ActPRM [1], while ActPRM itself trains a PRM on its full 663K pairs, and FARE-20B [2] is fine-tuned on about 600K step-level samples. Yet the gain is similar: on Hard2Verify, VerifySteer improves F1 by 9.6 on top of FARE-20B, close to the 10.1 gain from fine-tuning gpt-oss-20B into FARE-20B. Although we sample from an existing labeled dataset, this suggests that future verification datasets may need far fewer labeled examples. VerifySteer is also lightweight in compute, since it keeps the verifier frozen and trains only a small 3-layer MLP probe.

Our data is not sampled to match each benchmark. The correctness probe and the GSM8K vector use random ActPRM subsets, and OlympiadBench and Omni-MATH share one vector built from a random subset of the broad "olympiad" source of ActPRM. To show this further, in a new experiment, we show that the vector built from random data, which improves grade-school-level GSM8K, also transfers to olympiad-level Omni-MATH. It improves F1 over prompt optimization by 3.7, matching the 3.5 gain of the vector built from olympiad-level data.

Table 5. Transfer of the GSM8K (easy) steering vector to Omni-MATH (hard). Qwen3-8B on Omni-MATH split of ProcessBench.

MethodTNRTPRF1
Basic Prompt8.082.614.7
Prompt Optimization10.457.317.6
VerifySteer-Uni12.659.320.9 (+3.3)
VerifySteer-Uni w/ GSM8K vector12.458.920.5 (+2.9)
VerifySteer-Bi12.664.321.1 (+3.5)
VerifySteer-Bi w/ GSM8K vector12.961.421.3 (+3.7)

 


 

W2 The authors claim that the verifiers accept-or-reject tendency is encoded in the hidden state of the “\n\n” token, and that steering it also corrects the verifier’s reasoning. However, steering the first content token after the break gives similar gains, e.g., 76.0 vs. 76.4 F1 on MATH for Qwen3-8B (Table 4). So it is not clear whether the signal is specific to the paragraph break or is spread across nearby tokens.

We thank the reviewer for this question. We find that the signal exists around the paragraph boundary and it is strongest at \n\n. We have revised the introduction L93, contribution L114 to state this claim precisely.

This is supported by our ablation in Section 5.3 (Table 4). Steering at the first content token also improves F1 over prompt optimization, so the signal is not limited to the delimiter. However, steering at \n\n outperforms the first content token in all four settings (+1.7, +1.7, +2.2, and +0.4 F1), so the signal is strongest at \n\n. This extends prior work [3-4] on hidden-state steering, which focuses on \n\n alone.

Reference

[1] Duan et al. Efficient Process Reward Model Training via Active Learning

[2] Xu et al. Foundational Automatic Evaluators: Scaling Multi-Task Generative Evaluator Training for Reasoning-Centric Domains

[3] Chen et al. SEAL: Steerable Reasoning Calibration of Large Language Models for Free

[4] Zhang et al. Understanding and Steering the Cognitive Behaviors of Reasoning Models at Test-Time

 


 

Q2 Typos: L301: greedy decoding.Table 1 (space is missing) L373: "Our method keeps the verifier frozen. The verifier stays frozen throughout" -- repeats the same point

We thank the reviewer for pointing out the typos, and we fixed them in the revised paper.

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

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