acceptodds
Under review as a conference paper at ICLR 2027

Behavior Amplification: Discovering and Steering Model-Specific Reasoning Strengths in LLMs

Abstract

Recent work has advanced the ability of Large Language Models (LLMs) to reason about complex tasks. However, the majority of methodologies treat reasoning as a monolithic capability, whereas state-of-the-art models exhibit a high degree of diversity in their underlying reasoning behaviors. In this paper, we study how model-specific behavioral patterns are associated with success or failure in question answering. We propose a data-driven framework for discovering model-specific Behavioral Strength Sets: reasoning behaviors that are strongly correlated with answer correctness. These correlated behaviors are identified and selected via contrastive analysis and significance testing. Subsequently, we introduce Inherent Strength Amplification (ISA), a steering framework that leverages these behaviors to construct targeted interventions, including prompt injection, behavioral reflection, supervised fine-tuning (SFT), and reinforcement learning (RL). Across three model families and three question answering benchmarks, ISA consistently improves answer correctness over unsteered baselines, with gains of up to 41.0 EM and 29.2 F1 points. Our findings indicate that the effectiveness of each intervention depends upon the behaviors being amplified: behaviors that can be directly expressed as inference-time instructions are often improved through prompting or reflection, whereas behaviors requiring consistent multi-step execution derive greater benefit from parameter-level training. These outcomes demonstrate that effective reasoning improvement requires the alignment of interventions with a model’s specific behavioral profile, rather than the application of a universal optimization strategy.

Primary area:
generative models
Keywords:
Large Language Model Reasoning, Chain-of-Thought (CoT) Trajectories, Inherent Reasoning Capabilities, Reasoning Behavior Taxonomy, Model Steering & Alignment, Post-Training Adaptation, Post-Training Optimization

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_UHq4OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper asks whether different models have different effective reasoning behaviors. It induces candidate behaviors from correct and incorrect question-answering traces, labels their presence, and selects a model-specific Behavioral Strength Set using the difference in presence rates (Δ) and statistical tests. The authors then amplify these behaviors through prompt injection, behavioral reflection, supervised fine-tuning, or GRPO. Across nine settings spanning three open-weight models and three multi-hop QA benchmarks, the intervention selected on the discovery split improves over the baseline. The paper argues that the choice of intervention should match the type of behavior being targeted.

Critical strengths
  1. Valuable research question. The paper examines whether models have different effective reasoning behaviors and turns that idea into a measurable, actionable method. The question is clear and has practical value beyond applying the same reasoning strategy to every model.
  2. Broad experimental evaluation. The study covers three open-weight models, three multi-hop QA benchmarks, and four interventions, reporting EM/F1 and some confidence intervals. Volume-matched SFT and cross-model behavior-set ablations also probe the value of behavior-based selection and model specificity.
Critical weaknesses
  1. The reasoning is not fully justified. Behaviors that appear more often in correct traces are treated as model-specific reasoning strengths, and their amplification is taken to improve reasoning. Yet correlation does not establish that these behaviors cause correct answers. For example, explicitly committing to an answer may simply accompany a good answer. The current results do not adequately separate better reasoning from better answer presentation.
  2. The experiments do not fully support the proposed mechanism. Table 2 matches the number of ISA-SFT and vanilla SFT training examples but does not control for question difficulty, trace length, or answer format. In addition, the labeled discovery split is used both to induce candidate behaviors and to compute Δ. Without disjoint-sample validation and ablations by behavior category, alternative explanations involving data selection and sample reuse remain open.
Questions for authors
  1. Could the authors match question difficulty, trace length, and answer format when comparing ISA-SFT with vanilla SFT? How much gain remains when amplifying only answer-formation behaviors or only multi-hop reasoning behaviors?
  2. If candidate behaviors are induced and Δ is estimated on disjoint samples, how stable are the selected behavior sets and final gains?
2 comments
AuthorsOpenReview ↗

Responses to Reviewer UHq4

We appreciate the reviewer's positive assessment of the research question and the thoughtful comments.

W1 and Q1 (second question): Better reasoning or better answer presentation, and amplifying only one type of behavior.

To separate better reasoning from better answer presentation, we decomposed every test question that the selected intervention fixed, across all nine settings, by the quality of the baseline answer. A fix counts as a presentation fix if the baseline answer was already a near-match (token F1 ≥0.5\geq 0.5 but not an exact match), and as a substantive fix if the baseline answer was wrong in content (F1 <0.5< 0.5). 75% of fixes are substantive. Consistently, F1 gains track EM gains (+12.0 vs. +14.6 points on average), which would not hold if the gains came mainly from answer formatting. Gemma is the exception: most of its smaller gains on HotpotQA and MuSiQue are presentation fixes, which is consistent with its Strength Set consisting mainly of answer-formation behaviors (single-answer convergence, answer-minimization check).

ModelQuestions fixedSubstantive (baseline F1 <0.5< 0.5)Presentation (near-match)Δ\DeltaEMΔ\DeltaF1
Llama (3 datasets)10479 (76%)25+6.2+5.9
gpt-oss (3 datasets)180142 (79%)38+27.5+25.0
Gemma (3 datasets)6942 (61%)27+10.0+5.1
All nine settings353263 (75%)90+14.6+12.0

Behavior discovery identifies behaviors that are associated with correct answers, and the effect of amplifying them is then measured directly by the interventions on held-out questions. To check that the associations are not simply a by-product of question difficulty, we compared correct and incorrect traces only within groups of questions from the same dataset and of similar difficulty, measured by how many of the other models answer the question correctly. Within these groups, 14 of 15 Strength-Set behaviors keep Δ≥0.10\Delta \geq 0.10 and 13 of 15 remain significant after FDR correction. The gains of the steered models also hold on the hardest questions: on questions that no other model answers correctly, the selected intervention improves EM by 13.4 points (95% CI [10.4, 16.4]) across the nine settings.

Amplifying only reasoning or only answer-formation behaviors. We split each Strength Set into reasoning behaviors and answer-formation behaviors using a classification made by an independent LLM from the behavior definitions alone, and re-ran prompt injection on the test sets with each subset. These runs cover all nine settings, and we will share the results in a follow-up comment as soon as they are available.

W2 and Q1 (first question): Matching difficulty, trace length, and format in the SFT comparison.

We compared the ISA-SFT and vanilla-SFT training sets directly. They are matched in question difficulty (mean number of other models answering the question correctly: 2.6 vs. 2.6 for Llama, 2.2 vs. 2.1 for gpt-oss, 2.4 vs. 2.4 for Gemma) and in target length (median 686 vs. 668, 897 vs. 918, and 1,438 vs. 1,559 characters). Across models, both sets use identical prompt and answer formats and are drawn from the same model's correct training traces. Where example counts differ, the vanilla set is the larger one (gpt-oss +7%, Gemma +21%), which works against ISA-SFT rather than in its favor.

W2 and Q2: Disjoint validation, and stability of the selected behavior sets and final gains.

We recomputed behavior selection using only the 200-example train split of each model-dataset pair. All 15 behaviors in the paper's Strength Sets remain selected (Δ≥0.11\Delta \geq 0.11, FDR-adjusted q≤0.004q \leq 0.004), and 14 of 15 remain selected when Δ\Delta is computed within each dataset. Repeating behavior induction three times on different samples of discovery traces recovers 76% of the Strength-Set behaviors per repeat (12 of 15 reappear as essentially the same behavior at least once). For the final gains, selecting the intervention on one half of the held-out data and evaluating it on the disjoint other half (2,000 random splits) picks the same intervention in 100% of splits for all gpt-oss settings and Gemma/RAMDocs. Where selection varies (Llama), the candidates are near-tied and the chosen intervention trails the best by 3.7 EM on average.

I appreciate the authors' responses and clarifications. The rebuttal has addressed some of my concerns and improved my understanding of the paper. I have decided to raise my rating to 3.

Reviewer_AadHOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes discovering and amplifying model-specific behavioral strengths in multi-hop question answering. An LLM induces candidate behaviors from correct and incorrect traces, annotates their presence, and retains behaviors with a sufficiently large and statistically significant difference in presence between correct and incorrect outputs. The resulting Behavioral Strength Set guides four interventions: prompt injection, triggered reflection, behavior-filtered supervised fine-tuning, and GRPO initialized from that fine-tuned model. Intervention choice uses the discovery split, with final evaluation on a separate 200-example test split for each model-dataset pair. Across three open-weight models and HotpotQA, MuSiQue, and RAMDocs, the selected intervention improves EM in all nine settings; seven paired bootstrap intervals exclude zero. The paper also provides a volume-matched SFT control, cross-model steering, and annotation-robustness analyses.

Critical strengths
  1. The discovery-to-intervention workflow is concrete and produces substantial held-out gains. The open-weight results select interventions without using final test labels, and Table 6 provides paired uncertainty estimates instead of treating every positive change as significant. Some effects are large, including the gpt-oss RAMDocs EM increase from 19.0 to 60.0. The volume-matched vanilla SFT comparison in Table 2 also tests whether filtering correct traces adds value beyond the number of examples used.

  2. The appendix addresses several important annotation concerns. Behavior annotation excludes explicit correctness labels; a different-family judge yields overall Cohen's kappa of 0.71, and a reworded annotation prompt yields 0.86. Bootstrap reselection and FDR correction are reported. These checks strengthen confidence that the operational labels are not solely artifacts of one judge or prompt, even though they do not independently validate the proposed reasoning mechanisms.

Critical weaknesses
  1. Improvement over an unsteered model does not sufficiently establish the need for model-specific strength amplification. The donor-set and union controls are useful, but the reported average own-set advantages over the union in Table 3 are only 0.6 EM points for Llama and 0.5 for Gemma, without paired intervals. Individual datasets sometimes favor a donor set or the union. Behaviors such as answer commitment and context phrasing can improve output conformity without demonstrating stronger multi-step reasoning. The proposed distinction between instruction-expressible behaviors and behaviors requiring sustained execution is plausible, but model, behavior set, and intervention vary together, leaving that explanation unisolated.

  2. The strength-identification statistics reuse data involved in constructing the hypotheses. Figure 7 explicitly asks the induction model to identify behaviors occurring more frequently in correct traces, using labeled discovery examples. Section 3.3 then computes Z-tests on discovery plus training traces, including those same discovery examples. Annotation without outcome labels prevents one form of circularity, but does not remove this adaptive hypothesis-selection issue. FDR correction over the induced behaviors and bootstrapping a fixed schema do not establish independently calibrated significance for the entire discovery process. Moreover, the presence differences are pooled across datasets, so behavior-success associations may partly reflect dataset composition or difficulty. The held-out intervention results remain useful; the concern is specifically whether the retained sets are statistically established model-specific strengths.

  3. The large SFT regressions are not sufficiently diagnosed. Table 2 shows vanilla SFT reducing gpt-oss/HotpotQA EM from 62.0 to 37.0; on Gemma/MuSiQue, vanilla SFT and ISA-SFT reduce EM from 65.5 to 40.5 and 46.5, respectively. F1 also decreases substantially, so strict EM matching alone does not explain these results. Appendix G.1 discloses LoRA settings, a learning rate of 2e-4, 200 steps, and a 2,048-token sequence limit, but does not adequately document retained-example counts, truncation statistics, loss masking, or exact reasoning/answer serialization. Matching example counts and training budgets does not match difficulty, trace length, or formatting. Small-data overfitting, truncation, and format incompatibility remain possible explanations rather than established causes; the current evidence does not isolate the proposed behavior-to-intervention explanation from these training effects.

  4. Transfer of the discovered strengths to unseen datasets is not evaluated. The held-out tests establish generalization to new examples within HotpotQA, MuSiQue, and RAMDocs, but all three datasets contribute non-test traces to behavior discovery and statistical selection, and intervention choice uses each dataset's discovery split. The cross-model steering experiment tests donor behavior sets, not transfer to a dataset excluded from discovery. Consequently, the results do not establish whether the retained behaviors are stable model-specific strengths or habits useful for the evaluated task mixture. Appendix A acknowledges potential task-dependent behavior differences. A leave-one-dataset-out evaluation, fixing the behavior set and intervention using only the source datasets and applying them to the excluded dataset without target-label-based reselection, would directly test this distinction; transfer to an additional unseen QA dataset would provide stronger evidence.

  5. Competitive external prompting baselines are missing. The paper includes unsteered backbones, basic CoT for Llama, and useful internal ablations, but lacks comparisons with external reasoning-structure discovery, prompt optimization, and self-refinement methods. SELF-DISCOVER, GEPA, and Self-Refine would directly test whether model-specific behavior discovery adds value beyond existing approaches or additional inference calls. Comparisons should control the target model, supplied context, permitted non-test data, and inference budget, while reporting offline optimization costs separately. Relevant references are:

Questions for authors
  1. Specificity evidence: On the existing evaluation splits, how does own-set prompting compare with a generic grounding/concise-answer prompt of comparable length? Please report paired intervals for own-set versus union and donor-set differences in Table 3, and clarify whether the same example IDs are used across models. These results would materially affect the claim that model-specific discovery is necessary.

  2. Statistical clarification: If the schema induced on discovery is fixed, do the retained behaviors remain significant when presence differences and FDR correction are computed using only the separate training split? Please also show the associations within each dataset, rather than only pooled across datasets. This would distinguish independently supported strengths from adaptive selection or task-mixture effects.

  3. SFT diagnosis and reproducibility: What explains the large vanilla-SFT regression on gpt-oss/HotpotQA and the regressions of both SFT variants on Gemma/MuSiQue? Please report retained-example counts and length/difficulty distributions, the chat template and reasoning/answer serialization, loss masking, and consistent answer parsing across baseline and trained variants. What fraction of training sequences exceeds 2,048 tokens, and how are context, reasoning, and final answers handled during truncation? Training/validation curves and a targeted learning-rate or step-count check on these settings would help distinguish data suitability from training or formatting effects.

  4. Behavior naming and discovery stability: Are synonymous or overlapping candidate behaviors canonicalized or merged before annotation and statistical filtering? How are semantically similar behaviors compared across models? Please clarify whether induction uses one call or aggregates multiple calls, and whether repeating induction on the same discovery split yields comparable definitions and retained sets. The existing annotation-robustness checks use fixed definitions and do not answer this question.

  5. Reflection detector and cost: How is behavior coverage measured in the first-pass trace at inference time: by an LLM judge, signal-phrase matching, or another detector? Please specify its model/prompt or matching rules, and how missing behaviors are identified for the second pass. Please also report reflection-trigger frequency and additional annotation/generation calls or tokens, since conditional reflection saves cost relative to unconditional two-pass generation only after accounting for the coverage detector.

  6. Behavioral reward attribution: For the selected Llama/RAMDocs GRPO setting, does correctness-only GRPO from the same ISA-SFT checkpoint recover the gain, or does the behavioral reward add value? Given the phrase-based behavior score and its larger weight than correctness, how often do highly rewarded outputs contain the signal phrases without correctly performing the corresponding reasoning? This comparison would distinguish behavioral amplification from ordinary outcome optimization and surface-level reward exploitation.

4 comments
AuthorsOpenReview ↗

Responses to Reviewer AadH

We thank the reviewer for the detailed and constructive review, and for the concrete suggestions which we followed directly.

W1 and Q1: Specificity evidence (own set vs. union, donor sets, and a generic prompt) and whether the same example IDs are used.

Same example IDs. Within each target model, all behavior sets are evaluated on the same 200 test questions per dataset, so the comparisons in Table 3 are paired. Across target models the test questions differ, because splits are stratified on each model's own correctness.

Existing comparison, paired intervals, and a generic prompt. Table 3 already compares each model's own Strength Set with every other model's set and with the union, on the same test questions. For example, steering Llama with Gemma's set lowers its average EM from 40.8 to 27.0. We will share paired 95% confidence intervals for these differences, together with a new comparison against a generic grounding and concise-answer prompt matched in length to each model's Strength Set, in a follow-up comment as soon as they are available.

W2 and Q2: Statistical clarification (significance on the training split only, and associations within each dataset).

We fixed the candidate schema induced on the discovery split and recomputed Δ\Delta, the two-proportion z-tests, and Benjamini-Hochberg FDR using only the 200-example train split of each model-dataset pair. All 15 behaviors in the paper's Strength Sets remain significant and above threshold (Δ≥0.11\Delta \geq 0.11, FDR-adjusted q≤0.004q \leq 0.004).

Within each dataset separately (train split), 13 of 15 behaviors have positive Δ\Delta in all three datasets. The two exceptions are both chain-linking behaviors: Gemma's explicit chain linking (Δ=−0.01\Delta = -0.01 / 0.220.22 / 0.000.00 on HotpotQA / MuSiQue / RAMDocs) and Llama's chain of entity linking, which is positive on HotpotQA and MuSiQue (0.23, 0.26) but not on RAMDocs (−0.05).

ModelBehaviorΔ\Delta HotpotQAΔ\Delta MuSiQueΔ\Delta RAMDocs
Llamaexplicit answer commitment0.310.260.11
Llamachain of entity linking0.230.26−0.05
Llamaintermediate fact extraction0.260.180.19
Llamaquestion scoping0.180.140.05
gpt-ossdirect answer extraction0.150.490.07
gpt-ossmulti-hop chain resolution0.240.240.02
gpt-osscontext wording alignment0.110.190.08
gpt-osssingle entity focus0.320.180.04
Gemmasingle answer convergence0.200.290.29
Gemmaexplicit chain linking−0.010.220.00
Gemmaanswer minimization check0.270.210.05
Sonnetconfident answer convergence0.040.280.45
Sonnetdirect quote extraction0.080.050.19
Sonnetsingle chain resolution0.060.300.24
Sonnetunambiguous entity identification0.060.150.31

Averaging these within-dataset gaps across datasets, weighted by the number of traces in each (Mantel-Haenszel), 14 of 15 behaviors remain selected. We agree that pooled Δ\Delta can partly reflect dataset composition and will adopt the within-dataset statistic in the revision. Matching on question difficulty as well (the number of other models that answer the question correctly), 14 of 15 behaviors keep Δ≥0.10\Delta \geq 0.10 and 13 of 15 remain significant after FDR correction.

W3 and Q3: SFT diagnosis and reproducibility.

We are auditing the SFT pipeline along each of the dimensions the reviewer lists (retained-example counts, loss masking, sequence length and truncation, and answer parsing), and we are re-training the most affected setting with refined sequence handling. We will share the full diagnostics and the updated results in a follow-up comment as soon as they are available.

W4: Transfer to unseen datasets (leave-one-dataset-out).

We agree that a leave-one-dataset-out evaluation is a useful test of whether the discovered behaviors are stable strengths of a model or are tied to the evaluated task mixture. Our claims are scoped to the three multi-hop QA benchmarks we study, and the paper does not claim transfer to other domains (our limitations section notes that behaviors predictive on one dataset may not be equally useful on others). As a first check within the rebuttal period, we re-ran Strength-Set selection with each dataset held out in turn, computing Δ\Delta and significance only on the other two datasets' discovery and training traces. For Llama, the selected set is identical whichever dataset is held out. For gpt-oss it is identical when RAMDocs is held out and differs by one behavior otherwise, and for Gemma it is identical when MuSiQue is held out and drops one behavior otherwise. In these five unchanged cases, the reported test results on the held-out dataset involve no behavior selection on that dataset. We will make this scope explicit in the revision.

AuthorsOpenReview ↗

Responses to Reviewer AadH

W5: Comparisons with SELF-DISCOVER, GEPA, and Self-Refine.

We agree these methods are relevant, and we will discuss them in the related work. We have not run them within the rebuttal period, but they differ from our method in what they discover and use. SELF-DISCOVER has the LLM select and adapt generic seed reasoning modules (such as "Let's make a plan") into a task-level reasoning plan for new problem instances. These modules come from a fixed library, not from the model's own traces. Self-Refine has the model critique and revise its own output using generic self-feedback. Our behavioral reflection is the closest analogue, but its feedback targets the behaviors associated with the model's own successes, at a similar cost (about two generation calls per example, see Q5). GEPA optimizes a prompt through reflective, evolutionary search against a task metric. It may find instructions that steer the model toward particular behaviors, but it does not identify which behaviors characterize a model's successes, and its output is an optimized prompt rather than an interpretable behavior set that can also drive SFT and RL. The matched-length generic prompt in our response to Q1 tests the most direct form of the reviewer's question: whether discovered, model-specific behaviors add value beyond generic grounding and concise-answer instructions. We will share this comparison in a follow-up comment together with Q1 as soon as it's available.

Q4: Behavior naming and discovery stability.

Induction procedure. Induction is a single call to Claude Opus 4.6 per model at temperature 0. The prompt contains a sample of correct and incorrect discovery traces pooled across the three datasets, and asks for the most distinctive behaviors that appear more often in correct traces, each with a name, a one-sentence definition, and two example phrases signaling its presence and absence (Appendix). It returned five behaviors for each model. There is no separate merging or canonicalization step: the five candidates of a model are generated jointly in one call and passed directly to annotation and statistical selection. Behaviors are not canonicalized across models. Each model's set uses its own definitions, and cross-model comparisons (Table 3) steer each model with another model's definitions as written.

Stability under repeated induction. We repeated induction three times per model on different random samples of discovery traces (same prompt and temperature), and had an independent LLM judge, blind to which behaviors were retained, match each newly induced behavior to that model's original candidates from the definitions alone. Of the 60 new behaviors, 55 correspond to an original candidate of the same model (28 essentially identical, 27 overlapping but narrower or broader), and only 5 are new. On average, 76% of the Strength-Set behaviors reappear in each repeat, and across the three repeats 12 of the 15 Strength-Set behaviors reappear as essentially the same behavior at least once. Repeated induction therefore recovers largely the same behavior space, with variation mainly in naming and granularity (for example, Llama's chain of entity linking reappears as multi-hop chaining and chain linking entities).

Q5: Reflection detector and cost.

Behavior coverage in the first pass is measured by signal-phrase matching, not an LLM judge: a Strength-Set behavior counts as present if at least one of its signal phrases (short exemplars produced at induction) occurs in the first-pass trace (case-insensitive string match). If fewer than τm\tau_m behaviors are present (τm=3\tau_m = 3 for Llama and gpt-oss, 22 for Gemma, calibrated as the floor of the mean number of Strength-Set behaviors in correctly answered training traces), the second pass is run. The detector does not single out specific missing behaviors: the second-pass prompt lists all Strength-Set behaviors with their definitions and asks the model to regenerate its answer if any is missing, or otherwise confirm it.

Trigger frequency and cost. The detector adds no model calls. On the test sets, the second pass is triggered on 15% of examples on average (8% for Llama, 25% for gpt-oss, and 11% for Gemma), and reflection uses about 2.1×2.1\times the tokens of a single pass in total (range 1.9×1.9\times to 2.3×2.3\times).

Q6: Behavioral reward attribution in GRPO.

The behavior score counts a Strength-Set behavior as present when one of its signal phrases appears in the output. To check for surface-level exploitation, we compared how often signal phrases appear in the test-set outputs of the GRPO model and of the unsteered model. The rates are essentially the same (HotpotQA 24% vs. 26.5%, MuSiQue 16.5% vs. 16.5%, RAMDocs 18% vs. 16.5%), so the policy did not learn to insert signal phrases to collect reward. We agree that a correctness-only GRPO control from the same ISA-SFT checkpoint is the right comparison for isolating the contribution of the behavioral term.

Thank you for the additional analyses. The train-only checks and repeated induction address part of my concerns. However, several issues remain:

  1. Specificity: The matched generic-prompt comparison and paired own-set versus union intervals remain pending. These are central to establishing the value of model-specific discovery.
  2. Training attribution: The SFT diagnostics and updated results are not yet available, and the correctness-only GRPO control is still missing. Similar signal-phrase frequencies do not isolate the behavioral reward’s contribution.
  3. Transfer: Please clarify whether both candidate induction and intervention selection excluded the held-out dataset. Unchanged Strength Sets alone do not establish a fully held-out transfer evaluation.

These gaps still limit the attribution of the reported gains. Based on the evidence currently available, I maintain my original rating.

AuthorsOpenReview ↗

Follow-up to Reviewer AadH

Following up on our earlier response, we report the remaining analyses.

Specificity (W1 and Q1)

We computed paired bootstrap 95% CIs (10,000 resamples, stratified by dataset, n=600n = 600 questions) on the runs reported in Table 3, with the same scoring. For the generic comparison, we fixed a generic set before running any evaluation, with the same format and number of behaviors as each own set: context grounding, concise final answer, careful question reading and step-by-step reasoning (the first three for Gemma). We ran the generic set on the same test questions together with a fresh own-set run (averages within 1 EM point of Table 3), and the generic column compares with that run. Each cell is the own-set EM minus the EM with the other set, averaged over the three datasets.

Target (own EM)Other models' sets (mean)UnionGeneric
Llama (40.8)+8.4+8.4 [5.4,11.4][5.4, 11.4]+0.7+0.7 [−2.8,4.3][-2.8, 4.3]+4.0+4.0 [0.5,7.5][0.5, 7.5]
gpt-oss (47.0)+20.1+20.1 [16.6,23.6][16.6, 23.6]+23.2+23.2 [18.8,27.5][18.8, 27.5]−9.3-9.3 [−13.0,−5.7][-13.0, -5.7]
Gemma (63.7)+3.0+3.0 [1.2,4.8][1.2, 4.8]+0.5+0.5 [−1.8,2.8][-1.8, 2.8]+8.5+8.5 [6.0,11.2][6.0, 11.2]

Steering a model toward its own Strength Set outperforms steering it toward other models' sets for every model. For Llama and Gemma, the own set matches the union with a much shorter prompt. Against the generic set, the own set is higher for Llama and Gemma and lower for gpt-oss.

Training Attribution

  1. SFT diagnostics (W3 and Q3)

The ISA-SFT and vanilla-SFT sets are drawn from the same model's correct training traces and are matched in question difficulty (mean number of other models answering the question correctly: 2.6 vs. 2.6 for Llama, 2.2 vs. 2.1 for gpt-oss, 2.4 vs. 2.4 for Gemma) and in median target length (686 vs. 668, 897 vs. 918, and 1,438 vs. 1,559 characters), with 271 vs. 271, 431 vs. 462, and 225 vs. 272 examples. Each example (prompt, reasoning and answer) is trained as plain text without the chat template, with the loss over the full sequence and a 2,048-token limit applied from the end. For 24% to 36% of examples this limit removes some of the reasoning and answer, to a similar degree for both variants, so the ISA-SFT vs. vanilla comparison remains matched while the absolute SFT scores are affected. Re-evaluating the original vanilla-SFT gpt-oss model with our current pipeline reproduces the Table 2 result (38.0 EM and 50.0 F1 on the HotpotQA test set, vs. 37.0 and 50.9). A retrain with shortened contexts did not complete within the discussion period.

  1. Behavioral reward (Q6)

The correctness-only GRPO control could not be completed within the discussion period.

Transfer (W4)

We now also hold out intervention selection: for each held-out dataset, we pick the intervention with the highest discovery EM averaged over the other two datasets and evaluate it on the held-out test split. The pick matches Table 1 in 5 of 9 settings, the steered model improves over the baseline in 8 of 9, and the mean gain is +12.5+12.5 [10.5,14.5][10.5, 14.5] EM, compared with +14.6+14.6 [12.4,16.7][12.4, 16.7] with in-dataset selection. In five settings, the Strength Set is also unchanged when the held-out dataset is excluded (our earlier response), so both the behaviors and the intervention are chosen without it, and the mean gain is +11.7+11.7 EM. The one step that still sees the held-out dataset is candidate induction, where the LLM proposes candidate behaviors from traces pooled across all three datasets.

We hope these analyses address the reviewer's main concerns, and we would be grateful if the reviewer would consider updating their assessment.

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

This paper proposes a framework for discovering and amplifying model-specific reasoning behaviors in large language models. The authors first generate reasoning traces, then use Claude Opus 4.6 to induce candidate behavior taxonomies and annotate the presence of each behavior. Behavioral strengths are selected by comparing their occurrence rates in correct and incorrect traces, using a differential presence threshold and statistical significance testing. Based on the resulting Behavioral Strength Sets, the authors introduce ISA, which supports four interventions of behavior-guided prompting, behavioral reflection, ISA-SFT, and GRPO. Experiments across multiple models and question-answering benchmarks demonstrate that the proposed framework can consistently improve reasoning performance, although the effectiveness of different interventions varies across models and tasks. The paper also includes annotation robustness analyses, intervention-selection experiments, and cross-model behavior-steering ablations.

Critical strengths
  1. The paper proposes a pipeline that translates discovered behaviors into several concrete interventions, including prompting, conditional reflection, SFT, and RL. The comparison among interventions also provides insight into how the choice of steering mechanism may depend on the target model and behavior.
  2. The authors evaluate three open-weight models across three benchmarks and provide additional analyses of annotation agreement, prompt robustness, bootstrap stability, and cross-model behavior transfer. These analyses strengthen the empirical presentation, even though some important validity questions remain unresolved.
Critical weaknesses
  1. The proposed method identifies behavioral strengths by comparing behavior occurrence rates between correct and incorrect reasoning traces. However, the two groups may contain questions of substantially different difficulty, and the paper does not report repeated trajectories for the same questions. Consequently, the identified behaviors may reflect differences in question difficulty, context structure, or reasoning complexity rather than genuine reasoning strengths. For example, behaviors such as question decomposition and uncertainty expression may be more prevalent on difficult questions, regardless of whether they contribute to successful reasoning.
  2. The same discovery split is used for candidate behavior induction, statistical behavior selection, and final intervention selection. Since candidate behaviors are induced using correctness labels, reusing these samples for significance testing may inflate the estimated associations, which cannot be fully addressed by FDR correction or bootstrap stability analysis. Furthermore, selecting the best of four interventions on only 100 examples raises concerns about selection stability, especially when the top-performing methods differ by merely 1–2 EM points in Table 5. The authors should separate these stages using independent data or cross-validation and evaluate the stability of intervention selection across different splits.
Questions for authors
  1. Compared with Metacognitive Reuse[1], which component constitutes the main methodological advance?
  2. For behavioral reflection in Section 4, how is presence of each behavior detected at inference time to compute the trigger count relative to \tau_m?
  3. In Section 3.1, 500 examples per dataset are partitioned into 100 discovery, 200 training, and 200 test examples. How were these splits constructed, and why do the baseline numbers differ so drastically across splits of the same dataset?
    [1]Aniket Didolkar, Nicolas Ballas, Sanjeev Arora, and Anirudh Goyal. Metacognitive Reuse: Turning Recurring LLM Reasoning Into Concise Behaviors. arXiv:2509.13237, 2025.
5 comments
AuthorsOpenReview ↗

W1: Behaviors may reflect question difficulty, context structure, or reasoning complexity rather than genuine strengths.

We thank the reviewer for the careful review and the constructive questions on the validity of behavior selection.

We ran two analyses on existing traces.

(1) Difficulty-matched behavior selection. As a difficulty measure we use the number of the other three models that answer the same question correctly at baseline (0 to 3), excluding the model being analyzed. This measure captures difficulty well. For example, Llama answers 9% of the questions that no other model solves but 76% of those that all other models solve, so matching on it is a stringent test. To compare like with like, we grouped the training traces by dataset and by question difficulty (12 groups), measured the gap in behavior presence between correct and incorrect traces within each group, and averaged these within-group gaps, weighting each group by its number of traces (the standard Mantel-Haenszel estimate). A behavior that merely marks easy questions would show a large pooled gap but little or no gap within groups. 14 of 15 Strength-Set behaviors keep Δ≥0.10\Delta \geq 0.10, and 13 of 15 remain significant after FDR correction. Matching on context length as well gives the same 13 of 15. Both exceptions are Gemma behaviors (see W2). The associations are therefore not explained by question difficulty, dataset, or context length.

ModelBehaviorΔ\Delta (train)Δ\Delta matched on dataset ×\times difficulty [95% CI]q (FDR)
Llamaexplicit answer commitment0.270.26 [0.18, 0.35]< 0.001
Llamachain of entity linking0.280.12 [0.04, 0.19]0.002
Llamaintermediate fact extraction0.210.23 [0.16, 0.30]< 0.001
Llamaquestion scoping0.110.14 [0.09, 0.20]< 0.001
gpt-ossdirect answer extraction0.270.20 [0.10, 0.30]< 0.001
gpt-ossmulti-hop chain resolution0.250.14 [0.07, 0.20]< 0.001
gpt-osscontext wording alignment0.130.10 [0.03, 0.18]0.004
gpt-osssingle entity focus0.130.10 [0.01, 0.19]0.028
Gemmasingle answer convergence0.520.16 [0.05, 0.27]0.013
Gemmaexplicit chain linking0.570.04 [−0.05, 0.13]0.473
Gemmaanswer minimization check0.130.10 [−0.02, 0.23]0.200
Sonnetdirect quote extraction0.140.11 [0.06, 0.17]0.001
Sonnetsingle chain resolution0.470.14 [0.06, 0.22]0.001
Sonnetunambiguous entity identification0.440.15 [0.07, 0.23]< 0.001
Sonnetconfident answer convergence0.460.24 [0.15, 0.34]< 0.001

(2) Gains on hard questions. If certain behaviors were merely markers of easy questions, amplifying them should not help on hard ones. Binning the held-out test examples of all nine settings by the same difficulty measure, the selected intervention improves EM in every bin, including questions no other model answers correctly, and the gain is not concentrated on easy questions. Binning by the length of the model's own baseline reasoning trace gives the same picture. Excluding gpt-oss, whose gains are largest, every bin still improves with a confidence interval excluding zero (+5.4 to +13.5 EM).

Bin (all nine settings pooled)nBaseline EMSteered EMΔ\DeltaEM [95% CI]
No other model correct (hardest)5607.020.4+13.4 [10.4, 16.4]
1 other model correct36433.252.5+19.2 [14.0, 24.7]
2 other models correct37257.375.5+18.3 [13.2, 23.4]
All other models correct (easiest)50476.886.5+9.7 [6.0, 13.7]
Short baseline trace (bottom third)60349.859.9+10.1 [6.8, 13.4]
Medium baseline trace59444.861.1+16.3 [12.6, 19.9]
Long baseline trace (top third)60332.249.4+17.2 [13.4, 21.2]

We did not sample repeated trajectories per question. The difficulty-matched analysis addresses the same confound by contrasting correct and incorrect traces on questions of matched empirical difficulty. The held-out intervention results provide interventional evidence that complements this correlational analysis.

AuthorsOpenReview ↗

W2: Reuse of the discovery split and stability of intervention selection.

We thank the reviewer for the thoughtful review. The questions on difficulty confounds and on reuse of the discovery split led to the new analyses below.

(1) Behavior selection on independent data. We fixed the candidate schema induced on the discovery split and recomputed Δ\Delta, the two-proportion z-tests, and Benjamini-Hochberg FDR using only the 200-example train split of each model-dataset pair. All 15 behaviors in the paper's Strength Sets remain selected (Δ≥0.11\Delta \geq 0.11, FDR-adjusted q≤0.004q \leq 0.004). The only change is one additional Sonnet behavior that now also passes (stepwise question decomposition, Δ=0.12\Delta = 0.12). Because pooled associations could also reflect dataset composition, we additionally measured the gap between correct and incorrect traces within each dataset separately and averaged across datasets, weighting each by its number of traces (Mantel-Haenszel): 14 of 15 behaviors remain. We will adopt the within-dataset statistic in the revision. Held-out test gains are unaffected, since they are measured directly. We address question difficulty separately in our response to W1.

(2) Stability of intervention selection across splits. To use genuinely different data rather than resampling the same 100 examples, we repeatedly split each setting's 200 held-out examples into two disjoint halves (2,000 random splits). We selected the arg-max-EM intervention on one half and evaluated it on the other. This uses held-out labels only to measure stability, and Table 1 remains discovery-selected.

SettingTable 1 choiceMost often selected on a half (share of splits)Mean regret vs. best on other half (EM)
gpt-oss / HotpotQAISA-SFTISA-SFT (100%)0.0
gpt-oss / MuSiQueISA-SFTISA-SFT (100%)0.0
gpt-oss / RAMDocsISA-SFTISA-SFT (100%)0.0
Gemma / HotpotQAReflectionPrompt inj. (51%) / Reflection (49%), tied1.1
Gemma / MuSiQuePrompt inj.Prompt inj. (89%)0.7
Gemma / RAMDocsPrompt inj.Prompt inj. (100%)0.0
Llama / HotpotQAPrompt inj.ISA-SFT (59%)3.7
Llama / MuSiQuePrompt inj.GRPO (48%)3.7
Llama / RAMDocsGRPOISA-SFT (56%)3.6

Selection is stable wherever one intervention is clearly better (gpt-oss, Gemma). It varies only for Llama, where the top interventions are within about 4 EM of each other, so choosing among them costs at most about 3.7 EM on average.

AuthorsOpenReview ↗

Responses to questions from Reviewer CAea

Thank you for the detailed review and for recognizing the breadth of our evaluation.

Q1: Main methodological advance compared with Metacognitive Reuse.

The main difference between our paper and Didolkar et al. (2025) is how behaviors are discovered and selected. In that paper, the authors use a Reflection Prompt with a Metacognitive Strategist LLM to iteratively construct a behavior handbook: the Metacognitive Strategist is iteratively shown question, reasoning, and answer examples and is prompted to identify useful reasoning behaviors to add to the behavior handbook. Whether a behavior is useful is therefore decided by the LLM's judgment. In contrast, our method identifies useful behaviors via a systematic statistical analysis that correlates behaviors with answer correctness (effect-size threshold and significance tests with FDR control), yielding a model-specific Behavioral Strength Set. We then compare four steering mechanisms (prompting, reflection, SFT, and RL) and choose the mechanism for each model on held-out data, a choice that Didolkar et al. do not address. We will add this discussion to the related work.

Q2: How is behavior presence detected at inference time to compute the trigger count relative to τm\tau_m?

Detection is rule-based and requires no model calls. Each candidate behavior is induced in Stage 1 together with two short signal phrases taken from the traces (the induction prompt in the Appendix asks for "2 example phrases from the traces that signal its presence"). After the first pass, we count how many of the model's Strength-Set behaviors have at least one signal phrase in the first-pass trace (case-insensitive string match). If this count is below τm\tau_m, we run a second pass: the first-pass output is returned to the model with the Strength-Set behaviors and their definitions, and the model regenerates its answer if a behavior is missing. Otherwise, the first-pass answer is kept. τm\tau_m is calibrated on training data as the floor of the mean number of Strength-Set behaviors (judge-annotated) present in the model's correctly answered training traces (τm=3\tau_m = 3 for Llama and gpt-oss, 22 for Gemma).

Q3: How were the splits constructed and why do the baseline numbers differ across splits?

For each model-dataset pair, we label each of the 500 baseline traces as correct or incorrect from the model's own final answer (normalized exact match, or token-level F1 ≥0.5\geq 0.5 for near-matches).

The discovery split is deliberately balanced: we sample 50 correct and 50 incorrect traces, so that behavior induction and the correct-versus-incorrect contrast see equal numbers of each, even for strong models. For example, Gemma answers 86% of HotpotQA questions correctly, so a random 100-example split would contain only about 14 incorrect traces. The remaining 400 traces are shuffled and divided into train (200) and test (200). All splits are disjoint and fixed with seed 42.

This balancing explains the difference across splits. Every discovery split contains exactly 50 traces labeled correct and 50 labeled incorrect, while the train and test splits contain the remaining traces without balancing. Discovery baselines are therefore lower than test baselines for strong model-dataset pairs (Gemma/HotpotQA: 42.0 vs. 78.0 EM, Llama/HotpotQA: 36.0 vs. 49.5) and higher for weak ones (Gemma/RAMDocs: 23.0 vs. 19.5). Discovery EM is below 50% because the correctness label also credits near-matches that strict EM does not.

All four interventions are compared on the same discovery examples, and every reported result compares the baseline and the steered model on the same test examples. Our split-stability analysis (response to W2) shows that the selection is largely consistent when it is made on test data instead.

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

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