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Layer Agreement for Target Reformulation in On-Policy Distillation

Abstract

On-policy distillation (OPD) supervises a student on its own trajectories, but large teacher–student distribution gaps can destabilize direct alignment with the teacher's final predictions. This raises a target-construction question: what distribution should the student learn at its current state? We find that directional agreement between teacher and student probability revisions across layers is strongly associated with smaller final-distribution mismatch, providing evidence of local behavioral compatibility. Motivated by this observation, we propose Layer Agreement for Target Reformulation (LaTR), which uses layer evidence to construct an intermediate alignment target. At each student-visited prefix, target construction uses two signals. Teacher guidance uses the final teacher–student probability gap to specify each candidate token's correction direction. Layer evidence uses intermediate-to-final probability changes to assess both models' support for that direction. Combining these signals yields a bounded adjustment to teacher logits that reshapes both candidate-token selection and relative target probabilities. The student then aligns with a teacher-anchored distribution informed by both models' local behavior to mitigate alignment instability caused by large teacher–student distribution gaps. We evaluate three students across seven mathematical reasoning and code-generation benchmarks. LaTR achieves the best reported overall averages and code scores among compared methods, with gains over the strongest baseline of up to 3.81 percentage points in the seven-benchmark average and 4.70 percentage points on LiveCodeBench-v6.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Knowledge distillation, Layer-wise prediction dynamics, Target construction

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Reviewer_igaeOpenReview ↗
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Paper summary

This paper proposes Layer Agreement for Target Reformulation (LaTR), a method for improving on-policy distillation (OPD) by reformulating the teacher's target distribution using intermediate-layer information. Rather than directly matching the teacher's final-layer predictions, LaTR measures whether the teacher's and student's intermediate-to-final probability changes agree with the correction direction indicated by their final-layer probability gap. This layer-agreement signal is used to adjust teacher logits, construct a modified Top-K target distribution, and perform confidence-weighted reverse-KL distillation. Experiments on three Qwen student models across six mathematical reasoning benchmarks and LiveCodeBench-v6 show consistent improvements over Top-K OPD.

Critical strengths
  1. Reformulating the distillation target using teacher-student layer agreement is an interesting direction beyond conventional token selection or loss weighting.

  2. LaTR consistently outperforms the baselines across three student models on mathematical reasoning and code-generation benchmarks.

Critical weaknesses
  1. The motivation for using intermediate-to-final probability changes as indicators of supervision reliability could be further clarified. While the paper provides empirical evidence linking layer agreement to lower teacher-student divergence, it remains unclear why a student's internal probability revision in the teacher-preferred direction should imply that stronger supervision is beneficial. Conversely, a student whose internal revision opposes the teacher's correction may require stronger, rather than weaker, supervision. Further discussion or experiments connecting these revision patterns to actual learning outcomes would strengthen the motivation.

  2. The proposed reliability score and target construction require further justification. The asymmetric formulation in Eq. (3), particularly the different treatment of teacher-only and student-only support, appears heuristic and lacks sufficient justification.

  3. The OPSD baseline raises concerns about implementation fidelity and fairness. OPSD performs substantially worse than Top-K OPD on LiveCodeBench-v6. Given the performance reported in prior SDPO studies, the current performance is questionable.

Questions for authors

Please check the weaknesses above

Minor:

  • The term "Uniform" in Figure 6(e) and Appendix K may be misleading, as this baseline replaces intermediate-layer predictions with uniform distributions to retain the final-layer predictions. Consider renaming it to "Final-Layer Only" to better clarify the setting.
4 comments
AuthorsOpenReview ↗

Response to Reviewer igae

Thank you for the constructive feedback. We have addressed all comments in the revised manuscript and responses below.

All revisions have been incorporated into the updated PDF, and all responses and references below refer to this revised version.

W1: Layer-revision signals and beneficial correction directions

To test whether layer-revision patterns help determine beneficial target-correction directions, we added controlled interventions in Section 4.4, Table 3, with full settings and benchmark results in Appendix K, Table 19.

VariantControlled change and purposeSix-benchmark Avg
LaTRUses joint support and teacher-side conflict to determine candidate-level target corrections.46.25%
Support-flipReverses corrections on jointly supported candidates while preserving their magnitude, testing whether reinforcement is more beneficial than attenuation at these positions.44.53%
Conflict-upStrengthens teacher correction wherever the student's internal revision opposes it, testing whether these positions benefit from stronger teacher guidance.43.47%

The decreases connect correction direction to downstream learning outcomes. They support reinforcing jointly supported corrections and show that uniformly strengthening corrections under student opposition is less effectivethan LaTR's evidence-dependent treatment. LaTR adjusts candidate-level target probabilities, preserving teacher guidance when the teacher supports the correction and attenuating it when the teacher's own revision opposes it. These results support the proposed rule under the tested settings.

W2 : Justification for asymmetric treatment of one-sided support

To test whether teacher-only and student-only support warrant different correction rules, we added two targeted controls in Section 4.4, Table 3, with full settings and results in Appendix K, Table 19. Each changes only the corresponding one-sided treatment.

VariantControlled change and purposeSix-benchmark Avg
LaTRPreserves the teacher score under teacher-only support and attenuates it under student-only support.46.25%
Teacher-only softenWeakens corrections supported by the teacher but opposed by the student, testing whether student opposition alone justifies weakening teacher guidance.45.18%
Student-only retainPreserves the teacher score when the student supports a correction opposed by the teacher's own revision, testing whether attenuation is beneficial in this case.45.62%

The decreases support preserving teacher guidance when only the student disagrees and attenuating corrections opposed by the teacher's own layer evidence. These controlled comparisons provide empirical justification for distinguishing the source of disagreement in Eq. (3)'s asymmetric target construction.

The asymmetry reflects the teacher’s role as the supervision anchor. Student opposition may reflect knowledge not yet acquired, whereas teacher-side opposition indicates that the teacher’s own revision does not support the required correction.

W3 : Implementation fidelity and evaluation fairness

Thank you for raising this concern. We identified an error in our previous code evaluator: correctness was determined using a single public example rather than the complete test suite, inflating scores and compromising the comparison.

We corrected the evaluator and re-evaluated all methods under a common protocol. Appendix R.2 specifies the tool-assisted generation with 32 responses per problem. A response now counts as correct only if it passes all public and hidden tests using the official execution checker.

The corrected Table 1 reports:

StudentOPSDTop-K OPDLaTR
Qwen2.5-7B20.3223.1424.26
Qwen3-0.6B15.1516.5218.28
Qwen3-1.7B23.0226.7228.59

Q1 : Renaming “Uniform” to “Final-Layer Only”

We adopted this suggestion and renamed the control "Final-Layer Only" in the revised Figure 7(e), formerly Figure 6(e), and the corresponding tables and discussion in Section 4.4 and Appendix K. The description explicitly states that final predictions are retained while intermediate readouts are replaced with uniform distributions.

I appreciate the rebuttal. Although empirically observed, I am still not very convinced why and how does direction-aware fusion architecture work. Do the authors have any insight into this?

AuthorsOpenReview ↗

Response to Reviewer igae

Thank you for the follow-up. Our reasoning proceeds from what intermediate layers reveal, to why teacher–student compatibility matters, and finally to how these insights motivate LaTR’s correction rule. Intermediate predictions expose how token preferences develop, which we use to assess whether teacher guidance is supported by both models’ current predictive behavior.

1. Intermediate supervision constrains how predictions are formed. Patient Knowledge Distillation transfers information from multiple hidden layers, while OPRD aligns teacher and student representations on student-generated trajectories. OISD further supervises intermediate predictions and attention using the final layer. These studies report learning benefits from supervising internal representations or predictive behavior beyond final outputs ([1], [2], [3]). They motivate using intermediate information, without implying that layer alignment recovers a complete reasoning process.

2. Layer revisions reveal how token preferences develop. DoLa and SLED show that differences between intermediate and final predictions can improve output selection ([4], [5]). This motivates interpreting a probability revision as evidence of whether subsequent computation strengthens or suppresses a candidate. LaTR asks whether that revision supports the correction required by the final teacher–student gap. Agreement between the models alone is insufficient, since both could revise a token against the required correction.

3. Knowledge transfer also depends on compatibility. Rethinking OPD reports that successful transfer depends on both new teacher capabilities and compatible teacher–student generation patterns ([6]). Inspired by this distinction, we retain the teacher as the knowledge source and use the student’s revision as a local compatibility cue.

4. LaTR combines teacher knowledge with evidence of current compatibility. The final teacher–student gap specifies the required correction, while both models’ layer revisions indicate whether their predictive refinement supports that direction. When both support it, LaTR adds reinforcement because the teacher’s guidance is corroborated by both its own refinement and the student’s current predictive behavior. When only the teacher supports it, LaTR preserves the original teacher score because student opposition may reflect knowledge not yet acquired, rather than unsuitable guidance. When the teacher’s own revision opposes the correction, LaTR attenuates it because the teacher’s final preference relative to the student is not corroborated by its own refinement. The resulting rule preserves opportunities to learn new teacher knowledge while using compatibility evidence to determine additional reinforcement or attenuation. These bounded adjustments reshape candidate selection and relative target probabilities. The direction and asymmetry interventions in Section 4.4 and Appendix K support this interpretation in the evaluated settings.

[1] Sun et al. Patient Knowledge Distillation for BERT Model Compression. EMNLP-IJCNLP, 2019.

[2] Yang et al. OPRD: On-Policy Representation Distillation. arXiv:2606.06021, 2026.

[3] Liu et al. OISD: On-Policy Internal Self-Distillation of Language Models. arXiv:2605.29089, 2026.

[4] Chuang et al. DoLa: Decoding by Contrasting Layers Improves Factuality in Large Language Models. ICLR, 2024.

[5] Zhang et al. SLED: Self Logits Evolution Decoding for Improving Factuality in Large Language Models. NeurIPS, 2024.

[6] Li et al. Rethinking On-Policy Distillation of Large Language Models: Phenomenology, Mechanism, and Recipe. arXiv:2604.13016, 2026.

If any aspect remains unclear, we would be happy to provide further clarification.

AuthorsOpenReview ↗

Response to Reviewer igae

Dear Reviewer igae,

Thank you again for the time and care you have put into reviewing our submission. Your constructive feedback has helped us strengthen the paper.

With less than 8 hours left in the discussion period, we wanted to send a brief follow-up. For your question on the mechanism of our direction-aware fusion architecture, we explained it via intermediate-layer behaviors, teacher-student compatibility and LaTR’s correction rule, with supporting ablation results in Section 4.4 and Appendix K. We also grounded our reasoning in related works on intermediate supervision and layer-wise logit revision.

We would be grateful if you could let us know whether our responses have addressed your concerns. If any questions remain, we would be happy to discuss them.

Best regards,

The Authors

Reviewer_NnrpOpenReview ↗
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Paper summary

The paper addresses target construction in OPD when the teacher–student distribution gap is large. Two observational studies motivate the method. First, the directional agreement between teacher and student intermediate-to-final probability revisions over a shared candidate pool correlates strongly with final teacher–student KL (Spearman ρ ≈ −0.82). Second, this correlation weakens when the intermediate readouts are replaced with a uniform reference (ρ ≈ −0.74).

The proposed method, LaTR, works as follows:

  • At each student-visited prefix, the sign of the final probability gap sets a per-token correction direction st(v)s_t(v).
  • Each model's intermediate-to-final change (logit-lens readout at about 0.25 relative depth) measures support for that direction.
  • The adjusted logits re-select the Top-K support and reweight the target.
  • The student minimizes a reverse KL to this target, weighted by teacher confidence × retained mass.

Three Qwen students (0.6B–7B; Llama-3.1-8B in the appendix), six math benchmarks, and LiveCodeBench-v6 invloved in the experiment stage. The paper reports gains of up to +3.81 points (seven-benchmark average) and +4.70 points (LCB-v6) over the strongest baseline. Supporting material includes forced-replacement continuation studies, agreement tracking across training, a teacher-shift stress test, component and evidence-source ablations, and three bounds on target deviation, gradient perturbation, and retained teacher mass.

Critical strengths

Most OPD improvements change where or how strongly the student follows the teacher (token selection, weighting, divergence choice). This paper asks whether the teacher’s final distribution is the right target at the student’s current state. Using cross model layer revision agreement to reshape that target is, to my knowledge, new. It is also plugin and cheap: Table 23 shows the target can be combined with TIP and TA-OPD selectors. These include Real vs. Uniform vs. Shuffled evidence (Table 18) and removing the joint-support term, removing the teacher conflict term, or randomizing signs (Table 19). Randomizing signs while keeping magnitudes drops performance to roughly the baseline. This is the most convincing evidence that token aligned directional information, rather than an arbitrary bounded logit perturbation, matters. If the numbers hold up under multiple seeds, it would be a meaningful contribution.

Critical weaknesses
  • Several reported numbers cannot arise under the stated evaluation protocol. The math results are described as five-run means of pass@1. On AIME, with 30 problems, single-sample pass@1 per run makes many of the reported means unattainable (e.g., 26.73). It also makes the reported standard deviations below about 1.3 impossible, and many of the AIME entries fall in that range. In addition, two different metrics (five seed pass@1 and avg@32) give identical values for the same model on several benchmarks. AIME24 as consist with 30 questions as I know.

  • The separation from position weighting does not hold across models. On Qwen2.5-7B, most of the gain comes from target reformulation. On Qwen3-0.6B, however, target reformulation alone performs below the Top-K OPD baseline, and on Qwen3-1.7B position weighting contributes essentially nothing. The decomposition of the gains is therefore inconsistent across students. A simpler explanation is not ruled out. By construction, the adjustment moves the target toward the student whenever the teacher’s own layers oppose the correction. Much of the effect may therefore be generic target interpolation toward the student, similar in spirit to Veto. No control tests a constant magnitude gap shrinking adjustment, and Veto is not compared under the same support reselection. The motivating correlation may be largely mechanical. Roughly half of the prefixes have perfect agreement, plausibly low entropy positions where KL is trivially small. A uniform reference, which carries no intermediate-layer information, already recovers most of the correlation. The analysis does not control for teacher or student entropy or confidence.

Questions for authors
  • How exactly is pass@1 computed per seed? Please provide per-seed raw results for Table 1, and explain the attainability of the reported means and stds. Please also explain why the Qwen3-1.7B Vanilla avg@32 values in Table 24 coincide with the Table 1 pass@1 values. Which P is used for the main results (64 or 128)? Why does the same default configuration yield between 45.58 and 46.76 across tables?
  • Can you report the 2×2 ablation (target reformulation × position weighting) for all three Qwen students, with at least 3 seeds? How do you reconcile the Qwen3-0.6B result in Table 16 with the claim that most of the gain comes from target reformulation?
  • Can you add two controls: (a) a constant-magnitude gap-shrinking adjustment, η=−c st\eta = -c\, s_t, with the same re-selection; and (b) Veto with the same Top-K reselection?
  • What are the teachers’ own LiveCodeBench-v6 scores, and what problem date window and decontamination procedure were used? A distilled Qwen2.5-7B-Instruct reaching 58.87% avg@32 is unusually high. Was Vanilla also given the SFT stage applied to all distillation methods for code?
5 comments
AuthorsOpenReview ↗

Response1 to Reviewer Nnrp

Thank you for the constructive feedback. We have addressed all comments in the revised manuscript and responses below.

All revisions have been incorporated into the updated PDF, and all responses and references below refer to this revised version.

W1 & Q1 : Evaluation protocols, numerical consistency, and configuration clarification

Thank you for identifying these ambiguities. We have clarified the evaluation protocols and corrected the affected entries in the revised PDF.

1. Per-seed pass@1 and the reported means and standard deviations.

a^s=100N∑i=1Nci,s64\widehat{a}_s=\frac{100}{N}\sum_{i=1}^{N}\frac{c_{i,s}}{64}

where ci,sc_{i,s} counts correct responses among 64 samples for problem ii under evaluation seed ss. Table 1 reports the mean and sample standard deviation across five evaluation seeds for fixed trained checkpoints. The definition and table-specific sampling budgets are documented in Appendix R.1, Table 25.

The per-seed counts and scores for Qwen2.5-7B LaTR are provided below. Each seed entry shows correct responses / score (%).

BenchmarkProblemsResponses per seedSeed 42Seed 43Seed 44Seed 45Seed 46Mean ± sample SD (%)
AIME24301,920512 / 26.666667500 / 26.041667529 / 27.552083487 / 25.364583538 / 28.02083326.73 ± 1.08
AIME25301,920416 / 21.666667470 / 24.479167443 / 23.072917457 / 23.802083428 / 22.29166723.06 ± 1.13
AMC23402,5601,728 / 67.5000001,713 / 66.9140621,697 / 66.2890621,744 / 68.1250001,759 / 68.71093867.51 ± 0.96
MATH50050032,00026,098 / 81.55625026,177 / 81.80312526,256 / 82.05000026,414 / 82.54375026,335 / 82.29687582.05 ± 0.39
Minerva27217,4086,067 / 34.8517926,151 / 35.3343295,897 / 33.8752305,982 / 34.3635116,236 / 35.82261034.85 ± 0.77
OlympiadBench67543,20019,645 / 45.47453719,836 / 45.91666720,028 / 46.36111120,410 / 47.24537020,219 / 46.80324146.36 ± 0.70
Math macro-average (%)——46.28598546.74816946.53340146.90738347.32436146.76 ± 0.39

These per-seed counts reproduce the reported means and sample standard deviations, confirming their attainability under the stated evaluation protocol.

2. Identical pass@1 and avg@32 entries.

The four duplicated Qwen3-1.7B Vanilla entries in original Table 24, now Table 26, were copying errors. We have corrected them and the corresponding average:

BenchmarkCorrect / total responsesCorrected avg@32
AMC23741 / (40×32)57.89%
MATH50012,375 / (500×32)77.34%
Minerva2,701 / (272×32)31.03%
OlympiadBench10,984 / (675×32)50.85%

The corrected six-benchmark average is 44.85%. As clarified in Appendix R.1, avg@32 estimates the same single-response success probability using 32 responses per problem and one evaluation seed, whereas Table 1 uses 64 responses per problem across five evaluation seeds.

3. Candidate-pool size P.

The main experiments use K=32 and P=128. The earlier P= 2K, statement described an unused proposed setting and was mistakenly retained as the default. We have corrected Section 4.1 to match the actual experimental configuration.

4. Different default-reference scores across tables.

These values involved different evaluation budgets, an intermediate checkpoint, and a transcription error. The revised manuscript distinguishes them as follows.

Location: original → revisedOriginal valueExplanation and revisionRevised value
Table 1 → Table 1, Qwen2.5-7B LaTR math mean46.76%Full-budget checkpoint evaluated with 64 responses per problem across five evaluation seeds. Protocol clarified in Appendix R.1.46.76%
Tables 3, 19, 21 → Tables 4, 20, 22, and Fig. 6(c) → Fig. 7(c)46.25%Single evaluation with seed 42 and one response per problem. The evaluation budgets are summarized in Appendix R.1.46.25%
Table 17 → Table 18, teacher pool with both components enabled45.58%The original result used an intermediate checkpoint. Table 18 now reports matched full-budget component ablations, with the associated plot updated in Fig. 10.46.25%
Table 18 → Table 19, Real, now named LaTRAIME25: 23.00%, Avg: 46.75%AIME25 was mistakenly entered as 23.00% instead of 20.00%. We corrected the entry, average, and associated comparisons.AIME25: 20.00%, Avg: 46.25%

Here, 46.76% denotes Table 1's six-benchmark mathematical average, while its displayed Avg column includes all seven benchmarks. The single-evaluation reference of 46.25% follows the relevant tables' stated rounding convention. Therefore, the small differences arise from the different evaluation protocols and are within reasonable expectations. Comparisons within each experiment use matched evaluation settings.

AuthorsOpenReview ↗

Response2 to Reviewer Nnrp

W2 & Q2 & Q3 : Component contributions, alternative target rules, and signal validity

Thank you for identifying these concerns. The revised manuscript adds repeated evaluations, matched target-adjustment controls, and entropy/confidence-controlled analysis to address them separately.

1. Component contributions across students.

We report the complete 2×2 ablation in Appendix J, revised Table 17 (original Table 16). Each setting uses three seeds (42–44) under matched conditions. The six-benchmark averages are:

Target reformulationPosition weightingQwen2.5-7BQwen3-0.6BQwen3-1.7B
✗✗42.9540.8951.74
✓✗45.5941.8353.57
✗✓44.0941.4652.93
✓✓46.4042.8654.38

Target reformulation alone improves the averages by 2.64, 0.94, and 1.83 points, compared with 1.14, 0.57, and 1.19 points from position weighting alone. Adding position weighting to target reformulation contributes another 0.81, 1.03, and 0.81 points.

The original comparison used a single evaluation. Following your suggestion, the revised version uses 3-seed evaluation. The repeated evaluations show a positive standalone contribution from target reformulation on Qwen3-0.6B and a measurable contribution from position weighting on Qwen3-1.7B. We therefore refine our conclusion: target reformulation provides the standalone gain across these students, while both components contribute and their relative benefits vary across models.

2. Generic gap reduction and Veto with matched reselection.

To test these alternative explanations, we added both requested controls in Section 4.4, Table 3, with full settings and results in Appendix K, Table 19. All three methods share the candidate pool, Top-K reselection, normalization, and position-weighting rule.

VariantTarget construction and purposeSix-benchmark Avg
LaTRUses layer evidence to determine candidate-specific corrections.46.25%
Gap-shrinkApplies constant-magnitude logit corrections toward the student without layer evidence, testing generic gap reduction.43.62%
Veto-RApplies Veto's target-construction rule with the same Top-K reselection, testing an alternative adjustment under matched procedures.44.03%

LaTR improves the average by 2.63 and 2.22 points, respectively, and outperforms both controls on every benchmark. These comparisons support layer-conditioned target construction beyond constant-magnitude gap reduction at the tested scale and Veto's adjustment with matched reselection.

3. Low-KL prefixes and the uniform reference.

We agree that high-agreement, low-KL prefixes and shared final-distribution information may contribute substantially to the motivating correlation. This association alone therefore does not establish the value of intermediate-layer evidence.

The uniform reference retains the final predictions while removing actual intermediate information. Using actual intermediate readouts strengthens the agreement–KL correlation from −0.7359 to −0.8167, with a paired correlation-strength gain of 0.0808 and a 95% bootstrap interval of [0.0713, 0.0903] (Appendix F, Table 9). This supports additional diagnostic information relative to the final-only reference.

More directly, replacing intermediate readouts with uniform distributions during training (Final-Layer Only) reduces the six-benchmark average from 46.25% to 44.48%. Shuffling the evidence across candidate tokens reduces it to 42.45%(Section 4.4, Table 3, and Appendix K, Table 19). These controlled comparisons support the learning value of actual intermediate information and its correct token correspondence, beyond the motivating correlation alone.

4. Controlling teacher/student entropy and confidence.

To test whether layer agreement provides information about teacher–student divergence beyond entropy and confidence, we control both models' final-distribution entropy and maximum probability, together with prefix-context variables, on the same 6,600 prefixes. Figure 5 and Appendix F report the analysis.

AnalysisRank correlation95% confidence interval
Unadjusted−0.817[−0.828, −0.805]
Jointly controlling entropy, confidence, and prefix context−0.446[−0.478, −0.413]

The attenuation indicates that the controlled variables account for part of the original association. The remaining negative association supports additional diagnostic information from layer agreement under these linear rank controls, complementing the controlled learning experiments.

AuthorsOpenReview ↗

Response3 to Reviewer Nnrp

Q4 : Code evaluation validity, teacher scores, and SFT fairness

We identified and corrected a scoring error: the previous evaluator checked only a single public example instead of the complete test suite, inflating the reported scores. After re-evaluation, Table 1 reports 24.26% for Qwen2.5-7B LaTR, replacing 58.87%.

Appendix U, Table 27 reports the teachers' tool-assisted LiveCodeBench-v6 avg@32 scores:

Code teacheravg@32
Qwen2.5-Coder-7B-AgentRL-GRPO-TCR29.24%
Qwen3-GRPO_teacher-4B39.20%

Appendix R.2 details the corrected protocol. We use the Open-AgentRL-Eval 175-problem subset, dated January 4–April 6, 2025. Comparing normalized problem statements against Open-AgentRL-30K and the 3K SFT corpus removes seven matches and one related near-duplicate, leaving 167 problems. This addresses identified overlap with these corpora, while pretraining overlap remains unverified. Evaluation uses 32 tool-assisted responses per problem, and correctness requires passing all public and hidden tests with the official execution checker.

Section 4.1 clarifies that Vanilla receives no SFT. Format SFT is applied to both Qwen3 students before all distillation methods, but not to Qwen2.5-7B. Accordingly, Qwen3 comparisons against Vanilla reflect the combined training pipeline, while comparisons among distillation methods share the same SFT initialization.

Reviewer_5FRiOpenReview ↗
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Paper summary

In this paper, the authors proposed a new way of performing OPD. In vanilla OPD, the student generates prefixes and the teacher supervises the next-token distribution. The authors argued that when teacher and student are far apart in their layer-wise dustribution, the teacher's final layer distribution is a poor immediate target used by OPD. They first performed some preliminary experiments to show that there exists a student-teach layer-wise distribution gap, and then present their method LaTR, which incorporated the signal of model's intermediate-to-final probability change. Finally, they compared LaTR with several existing methods across three students on seven math and code-generation benchmarks, and showed that LaTR can obtain better performance on those tasks.

Critical strengths

The authors studied an interesting problem for OPD, and had conducted some empirical experiments to show the motivation of including extra signal of student-teacher agreement across intermediate-to-final layers during OPD. They have shown improvements over several existing methods on multiple models and benchmarks.

Critical weaknesses

I list the main concerns here and minor issues in the Questions for Author box.

  1. LaTR built on empirical results, and the authors did not prove strong evidence or insights on whether Eq. (3) and (4) are the best way to incorporate such student-teacher layer-wise signal in OPD. The authors also did not perform ablation studies or explain if other signals can be used to measure student-teacher distribution gap.
  2. The motivating experiments seems not strong enough. For example, the results in Table 7 in the appendix, it seems like half of the data has very low median KL values, so they actually agree with each other, then why the signal will be useful for OPD? Moreover, from Section 4.3, in Fig 4 (c ), the revision agreement only improves slightly over training steps, which did not support that including the signal helps mitigating disagreements.
  3. It is not clear after including the new layer-wise signal if OPD will be more stable or not. There is no strong theoretical support to explain LaTR will converge to a better optimum.
  4. In Section 2, the authors discussed more methods that tried to tackle student-teacher divergence, such as, TIP, Token Teachability, etc. But they did not compare LaTR with those methods.
  5. In Table 1, the variances are computed only based on evaluation seeds, but not on multiple training rounds. And other tables and figures reported results without variances, but they didn’t match the mean values reported in Table 1. Therefore, it is not clear if they use the fixed setup or not, the metrics varies all the times for the same model + task pairs.
Questions for authors
  1. Why does LaTR on Qwen2.5-7B score about 46.76 (Table 1) and 46.75 (Table 18) but 46.25 in Tables 3, 19 and 21 and Fig. 6(c)? Are these different runs, step budgets or configurations?
  2. Was Veto's β\beta schedule tuned with the same effort as γ0\gamma_0, KK, PP and readout depth? Does Top-K OPD in Table 1 also get the position weighting (Eqs. 6–7), to isolate target reformulation?
  3. Can you also show the teach model’s score in Table 1, so we know if the student models are well-trained?
6 comments
AuthorsOpenReview ↗

Response1 to Reviewer 5FRi

Thank you for the constructive feedback. We have addressed all comments in the revised manuscript and responses below.

All revisions have been incorporated into the updated PDF, and all responses and references below refer to this revised version.

W1 : Ablations of the reliability score and target construction

1.Empirical justification of the target construction.

We justify the proposed construction through component ablations and alternative correction rules. Our original submission included mechanism ablations, expanded in Section 4.4, Table 3, with full results in Appendix K, Tables 19–20.

Ablation groupVariantAvg (%)
ReferenceLaTR46.25
One-sided supportTeacher-only soften45.18
Student-only retain45.62
Group-specific directionsSupport-flip44.53
Conflict-up43.47
Alternative adjustment rulesGap-shrink43.62
Veto-R44.03
Evidence sourceFinal-Layer Only44.48
Shuffled42.45
  • Asymmetric treatment of one-sided support. Teacher-only soften tests weakening teacher-supported corrections when the student opposes them. Student-only retain tests preserving corrections opposed by the teacher but supported by the student. Their scores of 45.18% and 45.62% support preserving teacher guidance under student-only opposition and attenuating teacher-opposed corrections.
  • Learning value of the prescribed directions. Support-flip tests whether jointly supported corrections should be attenuated rather than reinforced. Conflict-up tests whether student opposition calls for uniformly stronger teacher guidance. Their lower scores of 44.53% and 43.47% favor reinforcing joint support and conditioning the treatment of student opposition on teacher evidence.
  • Additional value of intermediate information. Final-Layer Only tests whether final predictions alone suffice by replacing intermediate readouts with uniform distributions. Shuffled tests whether layer evidence remains useful without correct candidate-token correspondence. Their lower scores of 44.48% and 42.45% support using actual intermediate information with its correct token assignments.
  • Alternative target-adjustment rules. Gap-shrink tests whether simply shrinking the teacher–student gap, without layer evidence, explains the gains. Veto-R tests whether Veto provides a better adjustment rule under matched Top-K reselection. Their scores of 43.62% and 44.03%, compared with LaTR’s 46.25%, favor the proposed layer-conditioned construction over these alternatives.

Together, these interventions provide controlled empirical justification for Eqs. (3)–(4), supporting their effectiveness relative to the tested alternatives rather than universal optimality.

2.Alternative signals for diagnosing distribution mismatch.

Entropy and confidence also capture aspects of teacher–student mismatch, as examined in Figure 5 and Appendix F. Controlling both models’ entropy and maximum probability, together with prefix context, reduces the agreement–KL correlation from −0.817 to −0.446, indicating that these statistics explain part of the observed association. However, the remaining negative association (95% CI [−0.478, −0.413]) shows that layer agreement provides additional diagnostic information under these linear rank controls. Together with the learning ablations, this supports using layer evidence to construct supervision targets beyond the information captured by entropy and confidence.

Q3 : Teacher performance

We report task-specific teacher scores in Table 27. Teacher averages are 57.82% for Qwen2.5-7B and 61.34% for both Qwen3 students. Across seven benchmarks, the teacher–LaTR average gaps are 14.27, 21.92, and 10.72 percentage points for Qwen2.5-7B, Qwen3-0.6B, and Qwen3-1.7B, respectively. Prior OPD work also reports residual teacher–student gaps alongside substantial student improvements, suggesting that such gaps are reasonable. Such gaps can arise from smaller student model capacity or differences in pretraining.

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Response2 to Reviewer 5FRi

W2: Utility of layer agreement under low mismatch and modest agreement gains

We acknowledge that many prefixes in Table 8 (original Table 7), Appendix F, already have low teacher–student KL. However, our method does not require severe mismatch at every position. For candidate tokens whose final probability differences fall within the specified tolerance, the additional direct logit correction is zero. For candidates with remaining probability differences, we use both models’ layer evidence to assess whether their internal revisions support the required correction and construct the supervision target accordingly. Since OPD aggregates training losses across positions, improving supervision at a subset of positions can benefit overall learning. Thus, close alignment at many positions does not preclude the signal’s usefulness elsewhere. Its actual learning benefits need to be validated through controlled training experiments.

Regarding Fig. 4(c), we agree that the absolute increase in agreement is modest: from 86.30% to 87.78%, corresponding to an approximately 10.8% relative reduction in disagreement. However, our objective directly optimizes the student’s match to the adjusted target, rather than directly maximizing internal revision agreement. Using conflict information to improve supervision does not require all internal revisions to become aligned. The signal can help by changing how supervision is provided under conflicting revisions. We therefore interpret this curve as a supporting observation of training dynamics, rather than standalone causal evidence of signal effectiveness or conflict mitigation.

More direct support comes from the controlled training experiments and their downstream results in Section 4.4, Table 3, and Appendix K, Table 19:

  1. The value of intermediate-layer information and its token correspondence. Replacing actual intermediate predictions with a uniform reference (Final-Layer Only), or shuffling the correspondence between layer evidence and candidate tokens (Shuffled), reduces the six-benchmark average accuracy from 46.25% to 44.48% and 42.45%, respectively. These results support the value of actual, correctly token-aligned intermediate-layer information for target construction.
  2. The value of adapting supervision to support and conflict patterns. Reversing corrections jointly supported by both models (Support-flip), or uniformly strengthening teacher-directed corrections wherever the student’s revision opposes them (Conflict-up), reduces average accuracy to 44.53% and 43.47%, respectively. These results support using layer evidence to distinguish support from conflict and adjust supervision targets accordingly.

Together, these results support the conclusion that, in the evaluated settings, constructing supervision targets using actual layer evidence correctly associated with candidate tokens improves downstream OPD performance. This benefit does not depend on a large increase in global revision agreement.

W3 :Training stability and convergence guarantees

We address this concern through theoretical control of the correction and complementary measurements of training dynamics and performance across training seeds.

  • Theoretical control of the added signal. Our analysis in Appendix O bounds the adjusted target's KL deviation from the teacher on the selected support by γ2/2\gamma^2/2. At a fixed student state, support, and detached position weight, the additional local reverse-KL gradient with respect to student logits is bounded by wtγw_t\gamma. These results keep the target teacher-anchored and limit the local perturbation introduced by layer evidence.
  • Observed optimization stability. In the matched Qwen2.5-7B comparison, Appendix W, Table 29 reports a decrease in the 99th-percentile gradient norm from 3.322 to 1.835 and in late-stage AIME24 standard deviation from 3.44 to 1.70 percentage points, alongside higher mean accuracy. These measurements support reduced gradient extremes and stable late-stage performance.
  • Reproducible learning improvements. Across three paired Qwen3-0.6B training seeds, Appendix W, Table 30 reports 42.38 ± 0.52% for LaTR versus 40.00 ± 0.62% for Top-K OPD. LaTR achieves a higher six-benchmark average in every seed pair, with limited variation across its training runs. The controlled interventions in Section 4.4 and Appendix K further connect the chosen correction rules to improved downstream performance.

Together, the bounds provide a theoretical basis for controlling the intervention, while the training diagnostics and repeated training runs support stable optimization and reproducible performance improvements. The evidence establishes these empirical benefits, with the theoretical guarantees applying to target deviation and local gradient perturbation.

AuthorsOpenReview ↗

Response3 to Reviewer 5FRi

W4 : Comparisons with divergence-aware token-selection methods

We compare LaTR with entropy-based selection, TIP, and TA-OPD (token teachability) in Table 2, with full results in Appendix Q, Table 24 (original Table 23). Standalone LaTR achieves 46.25%, exceeding their respective averages of 45.88%, 44.15%, and 46.12%, demonstrating competitive standalone performance.

We also test whether LaTR complements token selection by retaining each method’s selected positions and applying LaTR’s target reformulation without its position weighting. This improves their averages by 1.34, 2.98, and 1.38 percentage points, respectively. These results provide the requested baseline comparisons and support the complementarity of layer-guided target construction with token selection.

W5 & Q1: Evaluation protocols, training variability, and cross-table consistency

Evaluation and training variability. Table 1 reports sample standard deviations across five evaluation seeds for fixed trained checkpoints. To additionally assess training variability, we report three paired training seeds for LaTR and Top-K OPD on Qwen3-0.6B in Appendix W, Table 30. Final checkpoints are evaluated using 32 responses per problem and fixed evaluation seed 42. LaTR achieves 42.38 ± 0.52%, compared with 40.00 ± 0.62% for Top-K OPD, with a higher six-benchmark average in every seed pair. These results support consistent performance gains across training randomness and limited variation across LaTR’s training runs.

Consistency across tables. Appendix R.1, Table 25 specifies the evaluation budgets: Table 1 uses 64 responses per problem and five evaluation seeds, Table 17 uses one response and three evaluation seeds, and single-evaluation ablations use one response with seed 42. Therefore, the small differences arise from the different evaluation protocols and are within reasonable expectations. Settings are matched within each ablation, while Tables 1, 17, and 30 separately assess evaluation or training variability. We also corrected a transcription error and replaced an intermediate-checkpoint result with matched full-budget results, as detailed below.

Location: original → revisedOriginal valueExplanation and correctionRevised value
Table 1 → Table 1, Qwen2.5-7B LaTR math mean46.76%Evaluated with 64 responses per problem across five evaluation seeds. This is the six-benchmark math mean.46.76%
Tables 3, 19, 21 → Tables 4, 20, 22, and Fig. 6(c) → Fig. 7(c)46.25%Evaluated with one response per problem and seed 42. This single-evaluation score need not equal Table 1’s repeated-evaluation mean.46.25%
Table 18 → Table 19, Real, now named LaTRAIME25: 23.00%, Avg: 46.75%A copying error entered 23.00% instead of 20.00% for AIME25. We corrected the entry and associated average and comparisons.AIME25: 20.00%, Avg: 46.25%
Table 17 → Table 18, teacher pool with both components enabled45.58%The original result used an intermediate checkpoint. We replaced it with matched full-budget component ablations and updated original Fig. 9 → revised Fig. 10.46.25%

Q2 : Veto tuning and isolation of target reformulation

Veto hyperparameter tuning. Readout depth, KK, PP, and γ0\gamma_0 are LaTR-specific parameters. Veto uses final-layer predictions and its own correction strength β0\beta_0. We added a validation search over β0∈0.1,0.3,0.6,0.8\beta_0\in\\{0.1,0.3,0.6,0.8\\} with constant or linear-decay schedules, plus a β=0\beta=0 reference (Appendix V, Table 28). All nine configurations use the same short training budget and held-out validation set. The search selects β0=0.6\beta_0=0.6 with linear decay to zero, which is used for the reported Veto results. This provides explicit tuning of Veto, although the search budgets across method-specific hyperparameters are not identical.

Isolation of target reformulation. Top-K OPD in Table 1 does not include the position weighting in Eqs. (6)–(7), as Table 1 compares complete methods. We isolate component contributions in revised Tables 4 and 17 (original Tables 3 and 16). Across the three Qwen students, target reformulation improves the six-benchmark mean by 2.64, 0.94, and 1.83 points without position weighting. With position weighting enabled in both compared variants, its gains are 2.31, 1.40, and 1.45 points. These controlled comparisons support target reformulation's contribution under both weighting settings.

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

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