acceptodds
Desk rejected at ICLR 2027

BoundaryEvo: Data-Model Co-Evolution at the Capability Boundary for Long-Chain Reasoning Distillation

Desk rejected at ICLR 2027, so left out of the paper lists and the map.

Abstract

Distilling long-chain reasoning trajectories from large teacher models provides an effective way to improve the reasoning ability of small language models. However, existing methods typically select a fixed training set before distillation, overlooking that the usefulness of a reasoning example changes as the student evolves. This mismatch becomes especially costly when only a small number of teacher trajectories can be used for training. Besides, examples already mastered provide little new supervision, while examples far beyond the capability of student may be difficult to learn from. Training data should therefore adapt as model capability evolves, yet reliable data selection is difficult when the student is initially weak. To address these challenges, our key idea is to first establish the basic reasoning capability and then adapt the training data to the evolving capability boundary of the student. We propose BoundaryEvo, a two-stage data–model co-evolution framework. In Capability Priming, we directly distill a small set of teacher-generated long reasoning trajectories without using a separate model to judge and filter them, allowing the student to acquire an initial reasoning capability before capability-aware data selection. In Capability-Boundary Co-Evolution, we repeatedly select questions that the current student has not mastered but the expert can reliably solve, and update the training data as the student evolves. With only 1,000 training examples, BoundaryEvo consistently outperforms static and dynamic data selection baselines across 11 reasoning benchmarks, raising the original Qwen3.5-4B accuracy from 62.9 to 75.3 on IMO-AnswerBench and from 26.8 to 46.0 on AMO-Bench. The code and data will be made publicly available.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Long-chain reasoning, Data-model co-evolution, Capability boundary, Knowledge distillation, Data-efficient learning

Reviews

Among:
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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_hyUoOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes BoundaryEvo, a distillation framework that combines knowledge distillation with curriculum learning for long-chain reasoning. Specifically, it studies how to iteratively adapt training data and distill teacher trajectories according to the evolving capability boundary of the student model, enabling the student to better acquire long-chain reasoning abilities. Using only 1,000 training examples, the method achieves strong improvements across 11 reasoning benchmarks—for example, improving Qwen3.5-4B from 79.8% to 92.5% on AIME25, from 62.9% to 75.3% on IMO-AnswerBench, and from 26.8% to 46.0% on AMO-Bench.

Critical strengths

Clear and well-motivated research direction. Existing distillation approaches typically rely on static data selection and lack a student-aware mechanism. This paper effectively captures this limitation by dynamically adapting the training data to the evolving capability boundary of the student model.

Critical weaknesses

1.Limited technical novelty and heavy engineering. Although the paper is packaged around the concept of the "capability boundary" (which has already been widely used to frame many existing works), the actual method is quite engineering-heavy. At its core, it essentially boils down to using an LLM-as-a-judge for data filtering and rejection-sampling SFT, combined with standard engineering tricks such as experience replay.

2.Lack of important baselines. The baseline comparisons are not comprehensive enough. In particular, the paper is missing comparisons against classic difficulty-based curriculum learning methods and standard pass@k-based rejection-sampling baselines, which are closely related to the proposed approach.

Questions for authors

Although the proposed pipeline is quite engineering-heavy, I still find this research direction meaningful. However, since the experiments in the paper rely on LoRA—which may introduce optimization bias—could the authors provide results with full-parameter fine-tuning to verify whether the conclusions still hold? In addition, could the authors compare against stronger baselines, such as a better-designed rejection-sampling SFT approach, and whether the multi-stage iterative training genuinely brings significant benefits compared to simply pooling all the selected data together and training in a single pass?

6 comments
AuthorsOpenReview ↗

Official Comment by Authors

Dear Reviewer hyUo,

We sincerely thank you for the insightful comments and constructive suggestions. We appreciate your recognition of our clear research motivation and the meaningful direction of adapting distillation data to the student's evolving capabilities. In response to your suggestions, we added difficulty-based curriculum learning, stronger rejection-sampling SFT, a same-data pooled control, and a first-update full-parameter comparison.

  • W1: Contribution.
  • A1:

We agree that LLM judging, rejection sampling, SFT, and replay are established components. Our contribution concerns which questions should receive a limited training budget as the student changes. Teacher verification determines whether a target solution is reliable; student-aware acquisition determines whether the corresponding question should be selected for the current student. BoundaryEvo couples repeated student–expert assessment with verified distillation and replay. We do not claim a new optimization objective or novelty for each component separately.

  • W2 / Q1: Stronger selection baselines.
  • A2:

To test the value of this acquisition procedure, we added two stronger baselines. Difficulty curriculum shares the candidate pool, quality filtering, and teacher verification; it estimates difficulty from the initial student's empirical success rates and fixes an easy-to-hard schedule. Strong RS-SFT uses the same teacher, per-question sampling cap, and verifier to obtain correct trajectories for quality-qualified questions, without student–expert gap selection. These controls test whether ordinary difficulty ordering or obtaining reliable targets alone suffices.

Table R1. Qwen3.5-4B LoRA results for difficulty curriculum, strong RS-SFT, same-data pooled training, and BoundaryEvo (scores in %).

Qwen3.5-4B / LoRAAIME25AIME26HMMT25HMMT26GPQA-D
Original model79.8084.0073.8068.9076.20
Difficulty curriculum84.1787.5082.5078.7978.28
Strong RS-SFT87.5090.0089.1777.2779.29
Same-data pooled80.0085.8375.8376.5276.89
BoundaryEvo (Turn3)92.5093.3090.0082.3081.30

BoundaryEvo has higher reported scores on all five tasks, by 3.02–8.33 percentage points over the curriculum baseline and 0.83–5.03 over strong RS-SFT. In particular, the AIME25 / GPQA-Diamond scores are 92.50 / 81.30 for BoundaryEvo, versus 84.17 / 78.28 for curriculum and 87.50 / 79.29 for RS-SFT. These results support an empirical contribution beyond applying the individual filtering and training components.

  • Q1: Iterative training versus pooling the acquired data.
  • A3:

For the pooled control, we collect the same 900 Stage 2 records acquired by BoundaryEvo across its three rounds, retaining replay multiplicities and the corresponding teacher trajectories. We then shuffle and train on this pooled multiset from the same Stage 1 checkpoint, with matched training exposure.

The pooled results are included in the table above. Iterative BoundaryEvo is higher on all five tasks, with differences of 12.50, 7.47, 14.17, 5.78, and 4.41 percentage points. This shows that simply pooling the acquired data does not match iterative training under the evaluated setup. These results indicate that multi-round training guided by student capability feedback provides gains over a single pooled training stage.

  • Q1: Full-parameter fine-tuning.
  • A4:

We compared BoundaryEvo with both RS-SFT and the LLM2LLM baseline under full-parameter fine-tuning, sharing the primed initialization and tuning budget. The following results are for one Stage 2 update:

Table R2. Full-parameter fine-tuning on Qwen3.5-4B: comparison after one Stage 2 update (scores in %).

Qwen3.5-4B / Full FTAIME25AIME26HMMT25HMMT26GPQA-D
Original model79.8084.0073.8068.9076.20
Stage 185.0087.5082.5069.7080.05
LLM2LLM (Turn1)85.8388.3382.5071.9779.92
RS-SFT (Turn1)86.6785.0083.3372.7377.78
BoundaryEvo (Turn1)89.1790.0087.5075.7680.30

Within full-parameter fine-tuning, BoundaryEvo exceeds RS-SFT by 2.50, 5.00, 4.17, 3.03, and 2.52 percentage points, and also exceeds the LLM2LLM baseline on all five tasks. This supports a conclusion with a defined scope: in the tested first-update setting, the observed acquisition advantage is not confined to LoRA.

Reviewer_hyUoOpenReview ↗

Follow-up

Thank you for the detailed response and the additional experiments. The stronger baselines and full-parameter fine-tuning results address several of my concerns and strengthen the empirical support for the proposed framework.

I would appreciate further clarification on the comparison between iterative and pooled training. Given that both settings use the same training records and teacher trajectories, the substantial performance gap is particularly noteworthy. Could you clarify what “matched training exposure” entails in practice? Specifically, are the total optimization steps and training-token budgets matched, and how are the learning-rate schedule, warmup, and optimizer states handled across the iterative rounds versus the pooled run?

These details would help distinguish the benefit of the round-wise training procedure from potential differences in optimization. Since the pooled control already uses data acquired by BoundaryEvo, I would also encourage a more precise interpretation of what this comparison establishes about iterative training versus dynamic data selection.

AuthorsOpenReview ↗

Replying to Follow-up Comment by Reviewer hyUo

Dear Reviewer hyUo,

Thank you for your thoughtful follow-up and for acknowledging that the stronger baselines and full-parameter fine-tuning results address several of your concerns. We appreciate your careful examination of the iterative-versus-pooled comparison. You are right that the optimization details are essential to interpreting this result. We have checked the saved training configurations and logs and recomputed the supervised-token counts. We clarify the comparison below.

  • Q1: What does “matched training exposure” mean, and are optimization steps and training tokens matched?
  • A1:

“Matched training exposure” refers to the same training-record multiset, teacher trajectories, and cumulative supervised-token exposure, all of which are identical between the two settings. Both settings start from the same Stage 1 merged checkpoint and process each of the 900 Stage 2 record occurrences for five epochs, preserving replay multiplicities.

Table F1. Actual configurations of the iterative and pooled Stage 2 runs.

SettingIterative trainingPooled training
Training records300 per round × 3 roundsThe same 900 records pooled together
Epochs5 per round5 over the pooled dataset
GPUs / per-device batch / gradient accumulation1 / 1 / 8 per round4 / 1 / 2
Effective batch size88
Optimization steps190 per round; 570 total565 total
Warmup steps19 per round; restarted each round57 once at the beginning
Peak learning rate1e-41e-4
Learning-rate scheduleThree separate warmup + cosine schedulesOne continuous warmup + cosine schedule
Optimizer stateReinitialized each roundPreserved throughout the pooled run
LoRA adapterMerged after each round; a fresh adapter is initialized for the next roundInitialized once and trained continuously
Reconstructed supervised response tokens105,064,215105,064,215

Both settings use LoRA rank 64 and alpha 128, a maximum sequence length of 40,960 tokens, bf16, and DeepSpeed ZeRO-3. The original iterative runs use replay/novel allocations of 150/150 in Turn 2 and 162/138 in Turn 3; these repeated records retain their multiplicities in the pooled dataset.

The five-step difference arises from the final incomplete batch of each epoch: iterative training uses 3 × 5 × ceil(300/8) = 570 updates, whereas pooled training uses 5 × ceil(900/8) = 565. Specifically, iterative training has 555 full batches and 15 four-record tail batches; pooled training has 560 full batches and five four-record tail batches.

The token counts were reconstructed from the saved datasets using the corresponding tokenizer, the qwen3 template, and the 40,960-token truncation rule. They count non-masked response-label tokens, including reasoning, final answers, and end-of-response markers, and exclude prompt and padding tokens. The three rounds contribute 37,568,965, 33,702,775, and 33,792,475 supervised tokens, respectively. None of the 900 records was truncated in this reconstruction. These are reconstructed supervision budgets, not measurements from a runtime per-batch token counter; Stage 1 is excluded because both runs share its checkpoint.

  • Q2: How are the learning-rate schedule, warmup, and optimizer states handled?
  • A2:

In iterative training, each round loads the preceding merged model weights and creates a new LoRA adapter and trainer, with resume_from_checkpoint: null. Previous LoRA updates are therefore retained in the model weights, but the adapter, optimizer moments, optimizer step counter, and learning-rate scheduler are reinitialized. Each round performs 19 warmup steps toward 1e-4, followed by cosine decay toward zero over its 190-step schedule.

The pooled run initializes its adapter and optimizer once, performs 57 warmup steps, and then follows a single cosine schedule over 565 updates, retaining optimizer states throughout. Consequently, the iterative setting returns to a higher learning-rate regime in later rounds, while the pooled learning rate continues to decay. We agree that these differences can affect the results even when cumulative supervised-token exposure and peak learning rate are matched.

Reviewer_bnyBOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

BoundaryEvo dynamically selects reasoning-distillation data as the student improves. It first primes the student with 100 unfiltered teacher trajectories, then performs three rounds of student–expert gap-based selection, verified teacher distillation, and replay. The method improves performance across 11 reasoning benchmarks and multiple student backbones with 1,000 cumulative training examples.

Critical strengths
  1. BoundaryEvo outperforms random and error-driven selection across all 11 benchmarks, with substantial mathematical reasoning gains.
  2. Cross-backbone results and ablations on priming, replay, and selection thresholds support the practical usefulness of the overall pipeline.
Critical weaknesses
  1. Expert success and student failure identify a performance gap, but do not establish that selected questions are near the student’s learnable frontier rather than simply difficult examples with reliable supervision.
  2. All evaluated students are in the 2B–4B range, leaving it unclear whether the selection strategy remains effective for larger, stronger students with narrower capability gaps to the expert.
Questions for authors
  1. Does boundary selection outperform student-error selection with identical quality filtering, teacher verification, and replay?
3 comments
AuthorsOpenReview ↗

Official Comment by Authors

Dear Reviewer bnyB,

We sincerely thank you for the insightful comments and constructive suggestions. We appreciate your recognition of BoundaryEvo's improvements over random and error-driven selection across all 11 benchmarks, and of its practical usefulness supported by cross-backbone results and ablation studies. To address your concerns, we added a controlled error-selection comparison, repeated-sampling measurements on selected questions, and an extension to a 9B student.

  • Q1: Comparison with matched student-error selection.
  • A1:

BoundaryEvo outperforms the highest-error selection control on all five evaluated tasks in the first-update comparison. The control selects the 300 questions with the highest student error rates. It shares the Stage 1 starting point, quality and validity filters, teacher verification, replay settings, and training budget with BoundaryEvo. Thus, the control also receives reliable teacher supervision; the comparison tests the additional value of the acquisition rule over prioritizing the student's most frequent errors.

Table R1. Matched first-update comparison on Qwen3.5-4B: highest-error selection versus BoundaryEvo (scores in %).

Qwen3.5-4BAIME25AIME26HMMT25HMMT26GPQA-D
Original model79.884.073.868.976.2
Highest-error 300 (Turn1)76.779.275.068.274.5
BoundaryEvo (Turn1)89.391.786.075.879.3

The gains over highest-error selection are 12.6, 12.5, 11.0, 7.6, and 4.8 percentage points, respectively. Under these matched conditions, simply prioritizing the most frequently failed questions is less effective than BoundaryEvo's selection.

  • W1: What the capability-boundary proxy establishes.
  • A2:

Our selection rule evaluates student and expert solution trajectories on the same candidate questions, alongside question quality and validity, before constructing verified teacher supervision. It therefore uses more information than a student-error ranking alone.

To characterize the selected data directly, we generated five solutions per question from both the student and teacher for each of the three selected batches and graded their answers:

Table R2. Student and expert accuracy on each selected batch, measured with five samples per question.

Selected batchStudent accuracyExpert accuracy
Turn 119.7%80.3%
Turn 225.3%82.8%
Turn 327.0%82.6%

These measurements show that the batches are challenging for the student while remaining substantially more solvable by the expert. The nonzero student success rates also show partial solvability at the batch level. This supports our operational description of an expert-solvable, student-unresolved region. The matched training comparison above provides complementary evidence of downstream utility. We will qualify the frontier terminology accordingly, rather than treating a performance gap as a proof of learnability.

  • W2: Extension to a larger student.
  • A3:

We extended BoundaryEvo to Qwen3.5-9B with the same expert, selection thresholds, and training-record budget. The results show improvements across all five tasks and all three evolution rounds:

Table R3. Qwen3.5-9B performance from the original model through Stage 1 and three evolution rounds (scores in %).

Qwen3.5-9BAIME25AIME26HMMT25HMMT26GPQA-D
Base Model90.0090.0083.2071.2081.70
Stage190.8390.0085.0079.5583.71
Turn191.6790.8388.3383.3383.84
Turn292.5094.1792.5084.8585.86
Turn3 (BoundaryEvo-9B)93.3396.6793.3387.8886.87

Relative to the original 9B model, the final gains are 3.33, 6.67, 10.13, 16.68, and 5.17 percentage points. This extends the empirical scope beyond the 2B–4B students and shows that the pipeline remains useful for this stronger student.

AuthorsOpenReview ↗

Looking forward to the reply

Dear Reviewer bnyB,

Thank you again for your time and constructive suggestions. In response to your comments, we have added a matched student-error selection comparison, measured student and expert accuracy on the selected questions, and extended our experiments to a 9B student. We have also clarified the interpretation of the capability-boundary proxy and incorporated these results and analyses into the revised manuscript.

As the discussion period approaches its end, we would greatly appreciate your feedback on whether these additions address your concerns about the selection strategy and its applicability to stronger students. We would be happy to answer any remaining questions.

Thank you again for your careful review and valuable feedback.

Authors of Submission 29943

Dear Reviewer bnyB,

Thank you again for your constructive feedback and recognition of our work’s empirical improvements. To facilitate your review as the discussion period draws to a close, we briefly summarize the additions addressing your concerns:

  1. Matched student-error selection: We added a first-update comparison sharing initialization, quality filtering, teacher verification, replay settings, and training budget. BoundaryEvo achieves higher reported scores on all five evaluated tasks (Appendix H.4).
  2. Characterizing selected questions: Using five solutions per question from the student and expert, we measured partial student solvability alongside substantially higher expert accuracy. We clarified that these measurements characterize the selected region rather than prove that every question lies at an optimal learnable frontier (Appendix H.4).
  3. Larger-student evaluation: We extended BoundaryEvo to Qwen3.5-9B with the same expert, thresholds, and training-record budget, observing improvements across all five tasks (Appendix H.5).

These experiments and clarifications are now included in the revised manuscript. We hope these additional results and clarifications strengthen your confidence in the effectiveness and broader applicability of BoundaryEvo. We would greatly appreciate your updated assessment in light of this evidence.

Thank you again for your time and thoughtful review.

Authors of Submission 29943

Reviewer_yMstOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies how to adapt the selection of long reasoning trajectories for distillation as the student model improves, under a small training-data budget. BoundaryEvo first primes the student with 100 teacher trajectories without additional model-based judging. It then performs three evolution rounds: the current student and a fixed expert answer the same candidate questions, and an analyzer evaluates their capability gap, question quality, and validity. Previously used questions that remain unresolved are prioritized for replay, alongside newly selected questions. Fresh teacher trajectories are then sampled for the selected questions, and only trajectories that pass final-answer verification are used for supervised fine-tuning. Each round uses 300 training records. The reported budget of 1,000 records is cumulative across rounds and includes replayed records.

The paper evaluates eight mathematical reasoning tasks and three general reasoning tasks on Qwen3.5-4B, with transfer experiments on Qwen3.5-2B and Gemma-4-E4B-it. Table 2 reports a final mathematical average of 76.4, compared with 67.7 for random selection and 70.0 for an error-driven selection baseline operating within the same fixed candidate pool. Ablations examine priming, verification during priming, replay, the number of evolution rounds, and the capability-gap threshold. The reported results are promising. However, the description of the common evaluation conditions and the evidence isolating the central mechanism of dynamic capability-boundary selection are not yet sufficient to support the paper's stronger conclusions.

Critical strengths
  1. The method addresses an important issue in practical distillation pipelines and separates question selection from solution supervision. Questions the student has not mastered do not necessarily have reliable teacher solutions; conversely, high-quality teacher solutions are not necessarily useful to the current student. The paper separates these considerations by using an independent expert to assess question-selection value, followed by fresh teacher trajectories and final-answer verification to construct supervision. Replaying previously used questions that remain unresolved also makes the procedure suitable for a continually updated student, beyond a single round of data filtering.

  2. The reported gains span multiple tasks and include validation across backbones. In Table 2, where the methods share the same Stage 1 starting point, the final method improves the mathematical average by 6.4 percentage points over the error-driven baseline, and raises IMO-AnswerBench from 67.4 to 75.3. The transfer experiments on Gemma also show substantial improvements (Table 3). Appendix C further examines generation length and finds a lower median reasoning length on all seven matched tasks, so the gains cannot simply be explained by a uniform increase in reasoning length. The paper also reports the 2B model's degradation in the third round, rather than presenting only cases of monotonic improvement.

Critical weaknesses
  1. It is unclear whether the central results were obtained under fully comparable evaluation conditions. Appendix G.1 (page 28, lines 1497–1503) explicitly states that Tables 1, 2, and 3 follow the same score-provenance rule: publicly reported results are used when available, with local evaluation otherwise. It subsequently describes a common protocol for controlled follow-up experiments, but does not identify which cells in the main tables come from those experiments. Interpreting the differences between the zero-shot and fine-tuned models in Table 2, as well as the large improvements in Table 3, requires evaluating them with the same prompts, numbers of completions, decoding configurations, and answer evaluators. Referring to EvalScope's default temperature/top-p without specifying the actual values and version does not allow this to be verified. I am not asserting that the comparisons are unfair; the current description makes it impossible to determine which conclusions may be affected by differences in provenance. The paper also does not report uncertainty across repeated training runs. Generating multiple completions for each question does not substitute for repetitions that vary the randomness of training and data selection.

  2. The existing controls do not adequately isolate the value of dynamic capability-boundary matching. Equation (5) and the rules in Appendix F.3 jointly introduce conditions on low student scores, high expert scores, question quality, and validity, while Table 2 primarily compares against random and error-driven selection. The resulting differences do not distinguish gains from dynamic capability matching from those due to more reliable expert solutions and stricter quality filtering. The static SFT result in Figure 4 covers only one task, and it is unclear whether it uses a frozen set selected with the same quality filters. The gap-threshold sweep in Table 5 does not replace this control. More specifically, the rule only requires a student score below 0.50, an expert score of at least 0.65, and a gap of at least 0.20. A question with a student score of 0 and an expert score of 1 therefore passes, so the rule does not directly exclude questions that are “far beyond” the student's capability, as discussed in the introduction. Changes in the mean scores of selected data in Figure 3 are also insufficient to establish that those questions lie near a learnable capability boundary. In addition, Appendix G.2 (page 29) states that the LLM2LLM baseline in the main tables is an adaptation and mentions a separate implementation of the original error-to-new-question synthesis procedure, but reports no results for it. The current evidence therefore supports the effectiveness of the combined pipeline more strongly than it establishes dynamic boundary re-estimation as the decisive source of the gains.

Questions for authors
  1. Please clarify the evaluation provenance of the main results. Has every row in Tables 2 and 3, including the original models, been re-evaluated under the common protocol described in G.1? If the controlled follow-up experiments are a separate set of experiments, please provide their results, along with the actual decoding parameters, the number of completions for each task, and the means and variability across repeated training runs. This clarification would directly affect my assessment of the reported improvements.

  2. How much does dynamic re-estimation itself contribute when teacher trajectories, quality and validity filters, replay budgets, and training configurations are held constant? Please compare against at least one strategy that freezes the initially selected set, and another that retains quality filtering without using the student–expert capability gap. Results for the LLM2LLM-style synthesis mentioned in Appendix G.2 would also help assess the advantage over existing methods, beyond fixed-pool error filtering.

  3. Does the Stage 1 verification ablation strictly match the amount of supervision and the question distribution? Does verified Stage 1 in Table 4 still contain 100 trajectories, and are they drawn from the same questions with comparable lengths and training-token counts? What proportion of the unverified data has incorrect final answers, as distinct from correct trajectories containing unsuccessful attempts? These details determine whether the results support the proposed explanation that preserving diverse exploratory behavior is beneficial.

4 comments
AuthorsOpenReview ↗

Official Comment by Authors

Dear Reviewer yMst,

We sincerely thank you for the insightful comments and constructive suggestions. We appreciate your recognition of the separation between question selection and solution supervision in our design, as well as the empirical gains across tasks and student backbones. We address your concerns below with explicit evaluation settings, additional acquisition controls, and an audit of the Stage 1 data.

  • W1 / Q1: Evaluation provenance and variation across training runs.
  • A1:

Every result in Tables 2 and 3 was evaluated locally under the common protocol, including the original models, Stage 1 checkpoints, evolution rounds, and selection baselines. Only some external comparison models in Table 1 use results cited from VibeThinker. We have explicitly clarified the evaluation provenance and corresponding source annotations in Appendix G.1 of the revised manuscript. Importantly, all within-backbone comparisons in Tables 2 and 3 are conducted under consistent evaluation conditions, ensuring that the reported improvements reflect methodological effectiveness rather than discrepancies in evaluation provenance.

We use EvalScope 1.10.0, with four independently sampled completions per question on every task. Scores average single-completion correctness, rather than selecting the best of four. Within each backbone, prompts, decoding settings, answer extraction, and evaluators are shared across checkpoints. The complete decoding settings for each backbone, including the additional Gemma sampling parameters, are now provided in a table in Appendix G.1 of the revised manuscript.

Separately from evaluation sampling, we repeated BoundaryEvo-4B training with four random seeds. We report the mean ± standard deviation (SD) across four training runs.

Table R1. Final BoundaryEvo-4B performance across four training runs (mean ± STD; scores in %).

Benchmark / aggregateMean ± STD
AIME2592.5 ± 0.9
AIME2693.3 ± 1.2
HMMT2590.0 ± 2.7
HMMT2682.3 ± 3.0
BruMO2595.8 ± 0.8
IMO-AnswerBench75.3 ± 0.4
AMO-Bench46.0 ± 3.2
ArxivMath35.9 ± 4.5
ZebraLogic96.0 ± 0.5
GPQA-Diamond81.3 ± 0.3
SuperGPQA55.0 ± 0.3
Math average76.4 ± 0.4
General average77.4 ± 0.2
  • W2 / Q2: Dynamic acquisition versus frozen data and quality filtering.
  • A2:

We added the three requested controls. Each method performs three sequential updates with 300 training records per update, continuing from the preceding checkpoint: 900 Stage 2 record slots in total, including repeated records. The fixed-pool comparisons share the candidate pool, quality and validity controls, teacher verification, and training settings.

Frozen-set reuses the initial selection for all three updates, testing whether repeated training on the initially selected data suffices. Quality-only retains quality filtering and teacher verification while removing student–expert capability matching from acquisition. LLM2LLM-style synthesis generates new questions from student errors, extending the comparison beyond the fixed-pool error-selection adaptation in the submitted tables.

Table R2. Acquisition strategies on Qwen3.5-4B after three updates of 300 records each (scores in %).

Acquisition strategyAIME25AIME26HMMT25HMMT26GPQA-D
Frozen-set88.3386.6787.5075.0076.52
Quality-only89.1791.6788.3381.0678.79
LLM2LLM synthesis89.1790.0087.5078.0378.03
BoundaryEvo92.5093.3090.0082.3081.30

BoundaryEvo has higher reported scores on all five tasks: gains are 2.50–7.30 percentage points over Frozen-set, 1.24–3.33 over Quality-only, and 2.50–4.27 over synthesis. These comparisons support the value of refreshing student-aware acquisition beyond repeatedly training on the initial set or retaining supervision-quality controls alone.

AuthorsOpenReview ↗

Official Comment by Authors

  • Q3: Stage 1 verification: matched questions and supervision audit.
  • A3:

Both groups contain 100 trajectories from exactly the same 100 question IDs, with the same initialization, training epochs, and optimization settings. Token exposure is comparable between the two groups: Verified has only 2.50% fewer loss-bearing response tokens per epoch.

The main observation is that Raw retains more trajectories with a correct final answer and unsuccessful attempts or explicit self-correction: 43% versus 21%, using all 100 trajectories in each group as the denominator. This is consistent with the interpretation that successful exploratory reasoning can be useful. The supporting audit is provided below.

Table R3. Stage 1 data audit: Raw and Verified trajectories from the same 100 questions.

Audit itemRawVerified
Questions / trajectories100 / 100100 / 100
Question IDs across groupsIdenticalIdentical
Loss-bearing response tokens / epoch1,477,9601,441,014
Truncated records7 / 1002 / 100
Correct answer with failed attempts/self-correction43 / 10021 / 100

Raw has 70 pass, 19 minor-error, and 11 major-error trajectory-level judge labels. The 43 successful exploratory trajectories were identified by an independent LLM annotation within the 70 pass trajectories.

AuthorsOpenReview ↗

Looking forward to the reply

Dear Reviewer yMst,

Thank you again for your time and constructive suggestions. In response to your comments, we have clarified the evaluation provenance and decoding settings, reported variability across four training seeds, added Frozen-set, Quality-only, and LLM2LLM-style synthesis comparisons, and audited the Stage 1 supervision and trajectories. These results and clarifications have been incorporated into the revised manuscript.

As the discussion period approaches its end, we would greatly appreciate your feedback on whether our responses and revisions address your concerns. We would be happy to provide any further clarification you may find helpful.

Thank you again for your careful review and valuable feedback.

Authors of Submission 29943

Dear Reviewer yMst,

Thank you again for your constructive feedback. To facilitate your review as the discussion period draws to a close, we briefly summarize the results and revisions addressing your concerns:

  1. Evaluation consistency: We clarified that all results in Tables 2 and 3 were evaluated locally under consistent within-backbone conditions. Appendix G.1 specifies decoding settings, four completions per question, and score aggregation.
  2. Training variability: We report BoundaryEvo-4B’s mean and standard deviation across four training seeds (Appendix H.2).
  3. Acquisition controls: We added Frozen-set, Quality-only, and LLM2LLM-style synthesis comparisons, with BoundaryEvo achieving higher reported scores on all five evaluated tasks (Appendix H.3).
  4. Stage 1 verification: We audited the same 100 questions in both conditions, documenting supervision-token counts and successful exploratory trajectories: 43% in Raw versus 21% in Verified (Appendix H.6). These results and clarifications are now included in the revised manuscript. We would appreciate any feedback on whether they address your concerns and would be happy to clarify any remaining questions.

Thank you again for your time and careful consideration.

Authors of Submission 29943

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General Response

General Description:

Dear Area Chairs and Reviewers,

We sincerely thank you for the time and effort devoted to reviewing our work. We greatly appreciate the constructive feedback from yMst (R1), bnyB (R2), and hyUo (R3), and your recognition of our work’s strengths, including (1) a meaningful and well-motivated research direction (R1, R3), (2) the separation of question selection from solution supervision (R1), (3) empirical improvements across tasks and student backbones (R1, R2), and (4) ablation studies supporting the practical usefulness of the pipeline (R2).

The main concerns focus on evaluation provenance and training variability (R1), the specific value and interpretation of capability-boundary selection (R1, R2), stronger baselines and the effects of iterative training and optimization choices (R3), and applicability to larger students (R2). We address these concerns through the following additional experiments and clarifications.

Additional Experiments and Analyses:

  1. Evaluation provenance and training variability — We clarify that all results in Tables 2 and 3 were evaluated locally under consistent conditions within each backbone. We provide the actual decoding settings in Appendix G.1 and report the mean ± standard deviation across four training seeds.
    References: R1: W1/Q1, Table R1; revised manuscript: Appendix G.1.

  2. Controlled comparisons of acquisition strategies — We compare BoundaryEvo against Frozen-set, Quality-only, and LLM2LLM-style synthesis. We also conduct a first-update comparison against highest-error selection with matched initialization, quality filtering, teacher verification, replay settings, and training budget. BoundaryEvo achieves higher scores on all five evaluated tasks in these comparisons.
    References: R1: W2/Q2, Table R2; R2: Q1, Table R1.

  3. Stronger baselines and iterative versus pooled training — We add difficulty-based curriculum learning and strong RS-SFT baselines, together with a pooled control using the same 900 Stage 2 records, preserving replay multiplicities and teacher trajectories. The results support the benefits of BoundaryEvo over these alternatives under the evaluated settings.
    References: R3: W2/Q1 and the iterative-training response, Table R1.

  4. Full-parameter fine-tuning — We compare BoundaryEvo with RS-SFT and LLM2LLM under full-parameter fine-tuning. BoundaryEvo outperforms both baselines on all five tasks after one Stage 2 update, showing that the observed first-update advantage is not confined to LoRA.
    References: R3: Q1, Table R2.

  5. Extension to a larger student — We extend BoundaryEvo to Qwen3.5-9B while retaining the same expert, selection thresholds, and training-record budget. Performance improves across all five tasks over three evolution rounds.
    References: R2: W2, Table R3.

  6. Analysis of selected questions and Stage 1 trajectories — We measure student and expert accuracy using five samples per selected question to characterize the acquisition region. We also audit the Stage 1 verification comparison, confirming identical question IDs and trajectory counts, and quantify correct-answer trajectories containing unsuccessful attempts or self-correction: 43% in Raw versus 21% in Verified.
    References: R2: W1, Table R2; R1: Q3, Table R3; revised manuscript: Appendices H.4 and H.6.

Revisions to the Manuscript:

We have incorporated the additional experiments and clarifications into the revised manuscript:

  1. Main paper: We added a dedicated subsection, “Data Selection Strategies and Full-Parameter Fine-Tuning,” with two tables reporting the difficulty curriculum, RS-SFT, same-data pooled, and full-parameter fine-tuning comparisons. The subsection explicitly describes the baseline definitions, comparison settings, and interpretation of iterative versus pooled training.

  2. Evaluation protocol: Appendix G.1 clarifies the provenance of the main results and provides the decoding settings and evaluation procedure. Appendix G.2 distinguishes the fixed-pool LLM2LLM adaptation from error-conditioned question synthesis.

  3. Additional experiments and implementation details: Appendix H.1 documents the iterative and pooled training configurations, including optimization steps, supervised-token budgets, learning-rate schedules, warmup, and optimizer and LoRA adapter state handling. Appendices H.2–H.6 present the four-seed variability analysis, additional acquisition controls, matched student-error comparison and selected-question analysis, 9B results, and Stage 1 data audit.

These revisions make the key comparison settings and results available in the main paper, with supporting details and analyses in the appendices. Thank you again for your constructive feedback and for helping us improve the clarity and empirical support of our work.

Sincerely,
Authors of Submission 29943

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