Question Begets Question: Self-Evolving Curriculum for Reinforcement Fine-Tuning on Competition Mathematics

Jianyou Wang; Longtian Bao; Ramamohan Paturi; Yang Zhang; Youze Zheng

REVIEW 3 major objections 5 minor 42 references

Question Begets Question: Self-Evolving Curriculum for Reinforcement Fine-Tuning on Competition Mathematics

T0 review · 3 major / 5 minor · reviewed 2026-08-06 · deepseek-v4-flash

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Pith's one-line read A self-evolving curriculum that regenerates problems from a model's near-successes lifts AIME pass@1 from 5.6% to 16.5% under a fixed data budget, with no plateau after 20 rounds.

desk verdict A clean ordering ablation shows a ~2-point pass@1 gain from curriculum organization, but unverified teacher answers and single-run arms keep the central claim from being fully nailed. read the letter →

arxiv 2608.01522 v1 pith:V76ATU5R submitted 2026-08-02 cs.LG cs.AIcs.CL

Longtian Bao , Jianyou Wang , Yang Zhang , Youze Zheng , Ramamohan Paturi This is my paper

classification cs.LGcs.AIcs.CL

keywords competitionmathematicsAIMEreinforcementfine-tuningcurriculumlearningsyntheticdataself-evolvingGRPOceilings

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

The paper studies why language models plateau when fine-tuned on hard reasoning tasks, using AIME competition problems as a controlled testbed. It introduces Question-begets-Question (QbQ), a teacher-driven generator that rewrites existing problems into diverse variants probing the same skill, and trains a 7-billion-parameter math model on those variants purely through reinforcement learning, never showing it the teacher's reasoning. The central finding is that the apparent ceiling is not fixed: when the same 6,000 QbQ problems are organized as a self-evolving curriculum that reseeds each round from problems the current checkpoint can mostly solve, pass@1 rises from 5.6% to 16.5%, with no saturation after 20 rounds, whereas shuffled static training plateaus at about 14.5%. A sympathetic reader should care because it suggests that for sparse-reward tasks without oracle reasoning traces, how training data is generated and sequenced may matter as much as how much data exists.

What carries the argument

Question-begets-Question (QbQ) is a teacher-driven generator that rewrites a seed problem along one of five structural operators — generalize-then-specialize, parametrize-and-sum, change the queried quantity, inverse, and add a constraint layer — so variants probe the same skill without being copies. The self-evolving loop scores every problem by the number of correct completions in 16 rollouts, keeps the band $8 \le n \le 15$ ('mostly right') as next-round seeds, and constructs the GRPO training set from variants whose empirical solve rate is closest to $1/2$, where the binary-reward group variance $\sqrt{\hat p(1-\hat p)}$ is largest. That selection rule is what makes the curriculum's rewa

What would settle it

Audit a random sample of the 6,000 QbQ variants by verifying their statements and final answers with an independent strong solver or human; if a nontrivial fraction are malformed or mis-answered, the reported gains would partly reflect reward noise rather than curriculum organization. Alternatively, rerun the 20-round loop with a different teacher model and check whether the mostly-right seed band still beats harder seeds.

Watch

Extended reading notes

Core claim

Under matched compute and data budgets, Qwen2.5-Math-7B's held-out AIME pass@1 can be raised from 5.62% to 16.46% by a 20-round curriculum in which each round evaluates the current checkpoint on the previous round's synthetic problems, seeds the teacher from the problems it solves 8–15 times out of 16, and trains only on the resulting variants' statements and final answers via GRPO. The same 6,000 problems, when globally shuffled and trained with the same 3,000 updates, plateau near 14.44%, and one-shot static augmentation reaches only 12.05%. The paper also reports that seeds from the mostly-right band outperform seeds from harder problems (16.46% vs 11.35%), and that the trained model gene

Load-bearing premise

The results assume that the GPT-5-mini-generated variants have correct statements and final answers, since training rewards compare the model's answer only to the teacher's answer and the paper reports no independent verification of the synthetic answers.

Editorial extensions

If this is right

Organizing the same synthetic data as a curriculum rather than shuffling it yields a 2.02-point pass@1 gain, isolating round ordering as the active ingredient.
Seeding from problems the model solves often but not reliably outperforms seeding from its hardest failures, contradicting the common mistake-driven synthesis recommendation.
Trained models transfer to hard problems never selected during training: pass@1 on 499 previously unsolved real AIME problems rises from 0.0% to 5.3%.
The absence of saturation after 20 rounds suggests the same budget could keep yielding gains with additional rounds.
The method requires only problem statements and final answers for training, never teacher reasoning traces, so it applies where oracle rationales do not exist.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

If the ceiling is set by training-distribution organization rather than model capacity, the same round-structured near-success seeding could transfer to other answer-checkable sparse-reward tasks where reasoning traces are absent, though the paper does not test this.
The variance-maximizing selection rule suggests a quantitative definition of 'mostly right': the productive band is where empirical solve rate is closest to 1/2, so the gain may be reproducible by directly filtering problems by solve rate instead of by round-by-round generation.
Because the teacher's answers are only checked for difference from the parent, adding an independent verification step for generated answers would make the method reliable in domains where wrong labels are costly; this is an engineering extension, not a claim of the paper.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

Short version: worth a serious referee. The headline result is a nice controlled comparison: same 6,000 QbQ problems, same optimizer, same 3,000 updates, only batch order changes, and pass@1 moves from 14.44 to 16.46 with small eval-seed error bars. That is a genuinely useful empirical finding. The operator-based QbQ procedure and the seed-band ablation (8–15 vs 1–7 vs 1–15) are also real contributions; the paper separates data generation from ordering and directly tests the “mostly right” hypothesis.

Soft spots, in rough order of weight. First, the generated-answer correctness assumption. The conclusion says “verified final answers,” but I could not find a verification step anywhere. Section 3.2 only filters variants whose answer differs from the parent; reward and band counts are computed against the teacher’s answer. If GPT-5-mini produces a nontrivial fraction of wrong answers, the GRPO reward is noisy and the seed-band counts are measuring “matches teacher” rather than “is correct.” This does not automatically kill the ordering result, since both arms see the same labels, but it could interact with selection and should be addressed with at least a sampled correctness check. Second, each arm is a single training run; the reported standard deviations are evaluation noise, not run-to-run variance. A 2-point gap is larger than the eval-seed sigma, but I would not call it conclusive until replicated. Third, no code or data is actually shipped in the arXiv version despite the claim that a code appendix exists. For a methods paper whose value is the recipe, that is a real deficiency. Fourth, the “no sign of saturation” claim rests on a 20-round window and should be phrased more cautiously.

None of these are fatal on their own. The core ablation is the right experiment and the result is plausible. What I would want from a revision: a validation check on generated answers, at least two or three training seeds per condition, and the code and data. The literature engagement looks fine; the references to Chen et al. and Liang et al. are appropriate and the claims about them are accurate.

Recommendation: send to peer review. The paper deserves a serious referee, and with the answer-verification issue addressed it would be a solid methods contribution. I would cite the ordering ablation in my own work.

Referee Report

3 major / 5 minor

Summary. The paper studies fine-tuning Qwen2.5-Math-7B on AIME competition mathematics, using only question–answer pairs and no teacher reasoning traces. It introduces QbQ, a GPT-5-mini-based procedure that transforms seed problems into variants via five structural operators, and a self-evolving curriculum that repeatedly selects seeds from the model's 'mostly right' band (8–15 correct out of 16 rollouts), generates 300 new variants per round, and trains with GRPO for 150 steps per round over 20 rounds. On held-out AIME 2025/2026, the curriculum reaches 16.46% pass@1, versus 14.44% for the same 6,000 QbQ problems trained in shuffled order and 12.05% for static augmentation, starting from 5.62% for the base model. The paper further reports a seed-band ablation showing mostly-right seeds outperform harder or mixed seeds, and a transfer result on 499 real problems that were never selected as seeds.

Significance. If the results hold, the paper makes a valuable contribution: it provides a controlled demonstration that, under a fixed data budget and fixed optimizer/update count, the organization of synthetic training data into a self-evolving curriculum can overcome an apparent learning plateau. The comparison between QbQ curriculum and QbQ non-curriculum is well designed, as it holds the problem multiset, initialization, optimizer, and number of GRPO updates fixed, and the held-out AIME 2025/2026 contests are not used for selection or stopping. The seed-band ablation and the transfer-to-hard-problems experiment are also informative. The main weaknesses are that the correctness of generated teacher answers is not verified, and each reported strategy is a single training run, so the headline gap is not yet supported by an estimate of training-run variance.

major comments (3)

[§4.1, Table 1, Figure 2] The reward in Eq. (1) and the solve counts n_t(q) used for band assignment and RL-set selection all compare the model's final answer to the teacher-supplied answer a_q. Section 3.2 describes only one filter for generated variants: the variant's answer must differ from the parent's answer. No correctness check of a_q is reported. If GPT-5-mini produces a non-negligible fraction of malformed statements or incorrect answers, then (i) the GRPO reward is corrupted, and (ii) the curriculum's seed-band and SelectRL criteria are systematically mismeasured. Because selection preferentially keeps variants with n_t(q) near k/2, an error mode in which the current policy happens to match a wrong teacher answer could create a spurious curriculum signal. The conclusion calls these 'verified final answers,' but verification is not described. I ask for independent verification (e.g., a symbolic/numeric s
[Appendix A, Table 2] Each strategy is a single training run; the reported standard deviations are over three evaluation sampling seeds only. The 2.02-point gap (16.46 vs 14.44) is large relative to the evaluation-seed standard deviations, but GRPO training is stochastic, and training-run variance is not measured. This is important because the seed-band ablation in Appendix A also appears to use one training run per arm, and those runs show substantial within-run fluctuations (e.g., the harder-seed arm reaches 14.17% midway and then declines; the mixed arm fluctuates between roughly 10% and 12.2%). Such volatility suggests that single-run comparisons may overstate the certainty of the curriculum's advantage. I recommend reporting results from multiple training seeds per arm, or otherwise providing a bound on training-run variance, before attributing the gain to curriculum organization.
[Figure 2] The statement 'no sign of saturation after 20 rounds' rests on the final portion of one training-run trajectory, and the intermediate points in Figure 2 are evaluated with a single sampling seed. The last two intervals (2,400→2,700→3,000 updates) show a rise from 13.58 to 15.77 to 17.08 on that curve, but the three-seed endpoint is 16.46±0.45. This supports 'continued improvement in this run,' but 'no sign of saturation' overstates the evidence unless more rounds or at least more evaluation seeds at intermediate checkpoints are provided.

minor comments (5)

[Abstract/§4.2] The abstract reports caps of 12.5% and 14.5% for static augmentation and non-curriculum QbQ, while Table 1 reports 12.05±0.34 and 14.44±0.61. These should be reconciled or explicitly labeled as trajectory peaks versus final checkpoints.
[§3.2] The Vendi-score comparison (1.59 vs 1.25) is described as 'after normalization,' but the normalization procedure is not specified. Please provide details or a reference so the reader can interpret the magnitude.
[§3.3] The format bonus b_i is added to the correctness reward before group normalization. Since the bonus is constant for all well-formed completions, it shifts the group mean but does not affect relative advantages among well-formed completions; the text could clarify this to avoid confusion about the bonus's role.
[Appendix C.1] The top-up rule uses variants with n_t=0 and then n_t=k as last resort. The paper says this top-up was never used. If true, stating it in the main text would be reassuring; if not, the RL-set construction differs from the stated protocol.
[§4.3] The transfer subset of 499 real problems is defined by M0's zero sampled accuracy and is drawn from the training pool, not from the held-out contests. This is a useful internal transfer check, but the label 'never seen during training' should be careful: these problems are in the AIME 1983–2024 pool, so they may have been seen during the SFT initialization, even if never selected in the curriculum loop.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: held-out evaluation is independent; seed-band choice is theoretically motivated and ablated; the only self-citation is illustrative, not load-bearing.

full rationale

The claimed derivation is not circular. The curriculum selects training problems using the model's own rollout solve counts n_t(q) (Algorithm 1), but the central comparison holds the 6,000 QbQ problems, initialization, optimizer, and update count fixed and changes only the round ordering (§4.1), while held-out AIME 2025/2026 performance is never used for selection or stopping (§3.4). The seed band B={8≤n≤15} is derived from a variance-maximization argument on the binary correctness reward (§3.3), not from the held-out outcome, and is tested against harder and mixed seed bands (Appendix A), so it is a motivated design choice, not a fitted prediction. The only self-citation (Wang et al. 2026) appears as an illustrative example of a domain without reasoning traces and is not load-bearing. The absence of verification of GPT-5-mini-generated answers is a correctness/validity risk (the GRPO reward may be noisy), but it is not circularity: the teacher answer is an input label, not the quantity being predicted, and the held-out official answers are independent of the training loop. No equation in the paper reduces to its own input by construction.

Assumptions & free parameters 4 free parameters · 3 assumptions · 0 invented entities

The central claim rests on synthetic data quality, the stability of difficulty measurement, and the AIME answer-format reward. None of these are independently verified beyond the paper's own filters and comparisons, so they are listed as domain assumptions rather than standard math.

free parameters (4)

seed band threshold (k/2 in pass@16 counts) = 8<=n<=15 for k=16
The seed band is chosen so rollout groups have nonzero reward variance (§3.3); the paper ablates it in Appendix A, so it is a deliberate hyperparameter, not fitted to held-out data.
variants per seed / waves = 3/3
Number of QbQ variants generated per seed per round; chosen for budget, not fitted.
RL-set size N = 300
Number of selected variants trained per round; budget-driven.
rounds T = 20
Fixed in advance; held-out performance never used for stopping.

assumptions (3)

domain assumption GPT-5-mini generated variants have correct statements and final answers
Used as ground-truth rewards in GRPO (§3.2, §3.3). No verification of generated answers beyond 'answer different from its parent' is reported; if incorrect, the reward signal is corrupted.
domain assumption Pass@16 with 16 i.i.d. rollouts at temperature 0.7 is an accurate difficulty estimate
Used to assign problems to seed bands each round (§3.1). The paper acknowledges re-measurement can move problems near band boundaries (Appendix C).
domain assumption AIME integer-answer correctness is a valid proxy for the target skill
The whole reward is exact final-answer match; this is the standard AIME evaluation protocol (§4.1).

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Cite this review

Pith. "Pith review of Question Begets Question: Self-Evolving Curriculum for Reinforcement Fine-Tuning on Competition Mathematics." pith.science (2026). https://pith.science/paper/V76ATU5R

@misc{pith2026260801522,
  author       = {Pith},
  title        = {Pith review of: Question Begets Question: Self-Evolving Curriculum for Reinforcement Fine-Tuning on Competition Mathematics},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/V76ATU5R}},
  note         = {Machine review of arXiv:2608.01522}
}

read the original abstract

Teaching a language model a skill it has not mastered is obstructed by three recurring difficulties: training data is scarce, ground-truth reasoning traces are usually unavailable, and models often exhibit an apparent ceiling beyond which additional data yields no further improvement. We study these difficulties in a controlled setting, fine-tuning Qwen2.5-Math-7B on competition mathematics (AIME), a task on which it initially solves only 5.6\% of problems (pass@1). To address data scarcity, we introduce Question-begets-Question (QbQ), a scalable procedure in which a teacher transforms existing problems into diverse variants that probe the same underlying skills; to model the absence of oracle reasoning, we train exclusively via reinforcement learning on problem statements and final answers, never on teacher reasoning traces. Static training on such data, however, plateaus well short of the task: real-plus-synthetic augmentation and non-curriculum QbQ generated synthetic data training cap pass@1 at 12.5\% and 14.5\% respectively, despite large increases in data. Our central finding is that this ceiling is not intrinsic to the model. We propose a self-evolving curriculum that, each round, evaluates the current checkpoint, seeds QbQ from the problems it can mostly get right, and trains on the resulting variants; under an identical data budget, this breaks the ceiling and lifts pass@1 to 16.5\% with no sign of saturation after 20 rounds. Counterintuitively, we find that models improve when trained on variants of problems they can mostly get right, and that models trained this way go on to solve harder problems never seen during training.

Figures

Figures reproduced from arXiv: 2608.01522 by the authors.

**Figure 2.** Pass@1 on AIME 2025 and 2026 during RL train [PITH_FULL_IMAGE:figures/full_fig_p006_2.png] view at source ↗

**Figure 3.** Held-out Pass@1 during training for the three seed [PITH_FULL_IMAGE:figures/full_fig_p010_3.png] view at source ↗

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Yue, Y.; Chen, Z.; Lu, R.; Zhao, A.; Wang, Z.; Yue, Y.; Song, S.; and Huang, G. 2025. Does Reinforcement Learning Really Incentivize Reasoning Capacity in LLMs Beyond the Base Model? arXiv:2504.13837

2025 arXiv
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Zhang, R.; Li, R.; Ma, Z.; Qiu, W.; Tao, C.; Wang, Y.; and Chu, X. 2026. D ^2 Evo: Dual Difficulty-Aware Self-Evolution for Data-Efficient Reinforcement Learning. arXiv:2605.17037

2026 arXiv

Pith tools

Reviewed August 6, 2026 · model on record in the stance chip above.

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Art of Problem Solving . 2024 b . USAMO Problems and Solutions. Art of Problem Solving Wiki, https://artofproblemsolving.com/wiki/index.php/USAMO_Problems_and_Solutions. Accessed 2026-07-29

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Bae, S.; Hong, J.; Lee, M. Y.; Kim, H.; Nam, J.; and Kwak, D. 2026. Online Difficulty Filtering for Reasoning Oriented Reinforcement Learning. arXiv:2504.03380

arXiv 2026

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Cai, P.; Fang, T.; Li, X.; Zeng, Q.; Li, G.; and Chen, J. 2026. Curriculum Reinforcement Learning Can Incentivize Reasoning Capacity in LLMs Beyond the Base Model. arXiv:2606.22317

work page Pith review arXiv 2026

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C.-Y.; Peng, B

Chen, J. C.-Y.; Peng, B. X.; Choubey, P. K.; Huang, K.-H.; Zhang, J.; Bansal, M.; and Wu, C.-S. 2026 a . Nudging the Boundaries of LLM Reasoning. arXiv:2509.25666

arXiv 2026

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Cog-DRIFT: Exploration on Adaptively Reformulated Instances Enables Learning from Hard Reasoning Problems

Chen, J. C.-Y.; Prasad, A.; Khan, Z.; Singh, J.; Tian, R.; Stengel-Eskin, E.; and Bansal, M. 2026 b . Cog-DRIFT: Exploration on Adaptively Reformulated Instances Enables Learning from Hard Reasoning Problems. arXiv:2604.04767

work page Pith review arXiv 2026

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Chen, X.; Lu, J.; Kim, M.; Zhang, D.; Tang, J.; Piché, A.; Gontier, N.; Bengio, Y.; and Kamalloo, E. 2025. Self-Evolving Curriculum for LLM Reasoning. arXiv:2505.14970

arXiv 2025

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arXiv 2021