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Under review as a conference paper at ICLR 2027

All Work And No Play Makes Jack a Dull Boy: Understanding and Preventing Catastrophic Strategy Collapse in RLVR

Abstract

During post-training of large language models (LLMs) with Reinforcement Learning with Verifiable Rewards (RLVR), GRPO-style algorithms can exhibit severe late-stage collapse. Prompt-based probing reveals that this is not benign strategic pruning, but a harmful contraction of effective strategy capacity that makes distinct reasoning strategies increasingly inaccessible. To characterize this phenomenon, we define strategies through trajectory-level policy-update interactions and develop a unified theoretical framework combining optimization dynamics and information theory. We prove that major RLVR objectives progressively concentrate probability mass onto a single strategy, while sustaining nontrivial task accuracy requires a minimum strategy capacity. The conflict between these two results provides a mechanistic explanation for catastrophic collapse. We further derive the Mirrored Entanglement Index (MEI) as a lightweight online warning signal. To prevent collapse, we propose Mesh Learning, which exposes multiple reasoning strategies and prevents any single strategy from dominating optimization. Across AIME26, AIME25, MATH-500, and GPQA, Mesh Learning consistently outperforms strong baselines across Qwen and Phi model families, with gains of up to 13.4 pp and 11.5 pp, respectively. These results establish strategy preservation as a key principle for stable RLVR. Code is available at https://anonymous.4open.science/r/Project1-060D.

Primary area:
learning theory
Keywords:
Reinforcement Learning, Reinforcement Learning with Verifiable Rewards, Large Language Models, Learning Theory, Optimization Dynamics, Information Theory, Reasoning, Strategy Collapse

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_JDskOpenReview ↗
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2(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies late-stage accuracy collapse in RLVR (GRPO/DAPO/GSPO, with and without KL/JS regularization). It defines a "strategy" as an equivalence class of trajectories with similar first-order coupling under policy updates, and shows empirically that these classes align with human-recognizable solution methods.

Critical strengths
  1. A coherent mechanistic story that connects theory, a measurable signal, and a fix. The optimizer-centric definition of a strategy (coupling-kernel equivalence classes) is a sensible way to lift trajectory-level updates to a replicator-type dynamics on strategies, and the "concentration vs. minimum capacity" contradiction is a clean explanation of why collapse is abrupt rather than gradual.

  2. The Coach-Prompting-only ablation (Table 2, "+CP" rows) is the right control: adding the same DeepSeek-generated prefixes to every baseline gives little or no gain, so the improvement is attributable to preserving strategies during optimization rather than to distilled priors from a stronger model.

Critical weaknesses
  1. Statistical reliability of the main table is not established. Results are Mean@4 with no seeds, no standard deviations, and no statement of how the reported checkpoint was chosen (final step vs. best step). This matters because AIME25/26 have 30 problems each, so one problem is 3.3 pp: many of the headline gaps (e.g., Qwen2.5-7B AIME26 13.3 vs. 10.0; Mesh m=3 vs. m=4) are within one or two problems.

  2. Evaluation protocol choices weaken the external validity of the gains. Qwen2.5-7B-Instruct is evaluated with a 1024-token cap on AIME (Table 5), which is far below what these problems need and makes the 3–13% numbers largely truncation-limited; Qwen3-4B thinking mode is capped at 8192 on AIME, well below its usual budget, so the reported baseline (13.3 / 21.6) is far from the model's known capability.

3,the inference-time protocol for Mesh Learning ("the policy proposes its own strategy and follows the same verification procedure") is not fully specified, and it is unclear whether baselines are evaluated with an identical prompt template and the same structured <thinking>/<Method Name> harness (App. D.1). If the template differs, part of the gain could come from the prompt rather than from the training method.

Questions for authors

Q1. How were the numbers in Tables 2–4 selected: final checkpoint, best checkpoint on the test set, or best on a held-out set? Please report per-method accuracy curves or best-step numbers for the baselines, plus std over seeds (or at least over the 4 samples).

Q2. Are baselines and Mesh Learning evaluated with exactly the same system/user prompt template at inference? Please show the exact inference prompt used for each row of Table 2.

Q3. Why a 1024-token generation cap for Qwen2.5-7B-Instruct on AIME? Could you add ablation experiment results

Q4. Strategy grouping for the regularizer: during training, is a rollout's strategy label simply the prefix it was conditioned on, or is it re-identified via the coupling kernel? If the former, how do you handle rollouts that ignore/switch the suggested strategy?

5 comments
AuthorsOpenReview ↗

Response to Reviewer JDsk [Part 1]

We respectfully thank the reviewer JDsk for recognizing the theoretical contributions of our work, particularly the concentration-capacity explanation of abrupt strategy/accuracy collapse, and for appreciating our ablation design. We also value the problems regarding experimental reliability and evaluation protocol, which we will address in the response below.

Note: We have uploaded a slightly revised manuscript with two minor updates: (1) clarifying the experimental protocol in Section 5.1, and (2) adding std@4 to Tables 2–4. The remaining experimental content is unchanged. Please refer to the latest PDF when assessing our responses.


To Q1: Checkpoint Selection and Training-Stage Comparisons

Tables 2–4 report the best checkpoint for each method, selected independently based on accuracy on the corresponding test benchmark. As already shown in Fig. 7, we provide training curves for all methods. On AIME25/26 and MATH, the baselines eventually collapse, with their final-checkpoint accuracy dropping to 0%. Therefore, we did not select the final checkpoints.

As for the variability of best-checkpoint result, we additionally report checkpoint accuracies throughout training for Mesh Learning and all compared baselines on AIME25/26, GPQA, and LiveCodeBench.

Specifically, we evaluate every 20 training steps, sampling four responses per question. Each 50-step interval reports mean accuracy and combined variability.

We use σreported=σstep2+σbetween2\sigma_{\text{reported}}=\sqrt{\sigma_{\text{step}}^2+\sigma_{\text{between}}^2}, where the step component uses Std@4, the dataset average of per-question correctness standard deviations across four responses. The between-checkpoint component measures variation of checkpoint Mean@4 within the bin. This is not a confidence interval.

As shown in these tables, Mesh Learning achieves the highest mean accuracy in almost every training stage after the initial 50 steps. Moreover, Mesh Learning continues training and generally maintains near-peak accuracy even after the baselines have collapsed. These results demonstrate that Mesh Learning's improvements are not simply an artifact of selecting the best checkpoint.

We will include these additional tables in the revised manuscript to make this comparison clearer.

AIME25 / AIME26 — Phi

Cell format: AIME25 / AIME26, mean ± std (%).

Step RangeGRPODAPOMesh Learning (Ours)
0–5018.9 ± 4.7 / 20.8 ± 1.515.8 ± 2.9 / 23.3 ± 0.820.0 ± 0.0 / 23.9 ± 1.3
51–10016.7 ± 0.8 / 17.8 ± 2.617.8 ± 2.6 / 24.0 ± 1.924.7 ± 1.3 / 28.9 ± 3.9
101–15018.3 ± 1.2 / 13.8 ± 0.613.8 ± 0.6 / 9.6 ± 11.227.9 ± 3.0 / 29.6 ± 3.0
151–20018.1 ± 1.0 / 9.4 ± 5.413.1 ± 1.3 / 0.0 ± 0.027.5 ± 0.8 / 30.5 ± 0.5
201–25017.5 ± 3.5 / 0.0 ± 0.012.9 ± 0.6 / 0.0 ± 0.027.1 ± 1.8 / 31.2 ± 0.6
251–30015.6 ± 1.3 / 0.0 ± 0.09.7 ± 2.4 / 0.0 ± 0.027.2 ± 1.3 / 31.9 ± 0.5
301–3509.2 ± 1.2 / 0.0 ± 0.04.6 ± 1.8 / 0.0 ± 0.027.5 ± 4.7 / 31.2 ± 0.6
351–4000.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.030.0 ± 1.2 / 31.2 ± 1.8

AIME25 / AIME26 — Qwen2.5-7B

Cell format: AIME25 / AIME26, mean ± std (%).

Step RangeGRPODAPOGSPOGRPO+KLGRPO+JSMesh Learning (Ours)
0–504.7 ± 2.7 / 7.8 ± 2.65.6 ± 1.3 / 3.1 ± 0.55.0 ± 1.9 / 0.0 ± 0.05.0 ± 3.8 / 3.2 ± 0.42.5 ± 2.5 / 0.0 ± 0.05.6 ± 1.9 / 7.5 ± 0.8
51–1005.6 ± 1.3 / 5.8 ± 0.80.0 ± 0.0 / 5.0 ± 0.02.8 ± 1.3 / 2.8 ± 0.00.0 ± 0.0 / 0.7 ± 0.10.0 ± 0.0 / 0.0 ± 0.08.9 ± 1.9 / 7.2 ± 0.5
101–1500.8 ± 1.2 / 7.1 ± 0.60.0 ± 0.0 / 2.9 ± 1.80.4 ± 0.6 / 2.9 ± 0.20.0 ± 0.0 / 0.6 ± 0.20.0 ± 0.0 / 0.0 ± 0.05.0 ± 2.4 / 8.5 ± 1.2
151–2000.0 ± 0.0 / 7.2 ± 1.00.0 ± 0.0 / 0.0 ± 0.00.3 ± 0.5 / 2.6 ± 0.10.0 ± 0.0 / 0.4 ± 0.70.0 ± 0.0 / 0.0 ± 0.012.2 ± 5.1 / 9.8 ± 1.7
201–2500.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.013.3 ± 3.3 / 10.3 ± 1.2
AuthorsOpenReview ↗

Response to Reviewer JDsk [Part 2]

AIME25 / AIME26 — Qwen3-4B

Cell format: AIME25 / AIME26, mean ± std (%).

Step RangeGRPODAPOGSPOGRPO+KLGRPO+JSMesh Learning (Ours)
0–5033.0 ± 7.1 / 32.2 ± 13.928.9 ± 9.9 / 33.3 ± 10.930.6 ± 11.4 / 32.8 ± 12.633.6 ± 8.0 / 31.1 ± 12.630.6 ± 10.5 / 28.9 ± 10.729.2 ± 9.2 / 28.3 ± 13.0
51–10034.7 ± 4.5 / 37.8 ± 1.933.1 ± 1.7 / 36.9 ± 3.435.0 ± 3.0 / 39.4 ± 2.132.7 ± 6.1 / 37.8 ± 6.935.3 ± 2.8 / 33.3 ± 5.843.3 ± 5.0 / 43.9 ± 5.1
101–15017.7 ± 14.1 / 25.0 ± 11.838.8 ± 6.5 / 40.0 ± 4.74.6 ± 6.5 / 7.5 ± 10.611.7 ± 15.4 / 16.7 ± 18.933.3 ± 12.6 / 11.7 ± 16.545.8 ± 3.5 / 49.6 ± 4.1
151–2000.3 ± 1.1 / 0.0 ± 0.023.9 ± 21.3 / 32.5 ± 5.10.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.045.0 ± 4.4 / 50.0 ± 6.7
201–2500.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.00.0 ± 0.0 / 0.0 ± 0.046.7 ± 0.0 / 45.0 ± 2.4

GPQA — Phi

Accuracy: mean ± std (%).

Step RangeGRPODAPOMesh Learning (Ours)
0–5014.3 ± 4.014.3 ± 4.014.3 ± 4.0
51–10016.5 ± 1.821.8 ± 6.021.8 ± 6.0
101–1506.8 ± 9.10.0 ± 0.031.8 ± 2.1
151–2000.0 ± 0.00.0 ± 0.030.4 ± 3.5
201–2500.0 ± 0.00.0 ± 0.027.6 ± 0.5

GPQA — Qwen2.5-7B

Accuracy: mean ± std (%).

Step RangeGRPODAPOGSPOGRPO+KLGRPO+JSMesh Learning (Ours)
0–5028.0 ± 7.223.8 ± 5.326.2 ± 10.624.1 ± 6.315.6 ± 11.027.3 ± 5.8
51–10032.3 ± 1.532.1 ± 0.732.8 ± 1.227.9 ± 1.80.0 ± 0.030.1 ± 1.7
101–15031.3 ± 0.631.2 ± 1.329.8 ± 1.520.1 ± 7.70.0 ± 0.031.5 ± 1.4
151–20029.9 ± 0.930.4 ± 1.631.3 ± 1.030.3 ± 2.00.0 ± 0.033.4 ± 1.8

GPQA — Qwen3-4B

Accuracy: mean ± std (%).

Step RangeGRPODAPOGSPOGRPO+KLGRPO+JSMesh Learning (Ours)
0–5019.4 ± 7.321.7 ± 9.617.9 ± 6.621.6 ± 9.028.1 ± 15.228.2 ± 12.7
51–10033.9 ± 3.143.1 ± 0.741.3 ± 3.039.9 ± 1.740.7 ± 3.644.7 ± 2.5
101–15036.0 ± 0.043.2 ± 1.943.7 ± 1.638.8 ± 2.733.4 ± 0.144.4 ± 1.2
151–20035.9 ± 1.642.8 ± 1.242.4 ± 1.040.4 ± 1.90.0 ± 0.045.4 ± 2.2
201–25037.0 ± 1.742.5 ± 1.30.0 ± 0.039.1 ± 2.60.0 ± 0.044.0 ± 0.2
251–30037.2 ± 2.541.6 ± 0.50.0 ± 0.040.4 ± 0.30.0 ± 0.043.0 ± 0.1

LiveCodeBench — Phi

Accuracy: mean ± std (%).

Step RangeGRPODAPOMesh Learning (Ours)
0–5027.7 ± 3.128.5 ± 4.433.8 ± 5.6
51–1000.0 ± 0.00.0 ± 0.032.5 ± 2.3
101–1500.0 ± 0.00.0 ± 0.033.7 ± 2.9

LiveCodeBench — Qwen3-4B

Accuracy: mean ± std (%).

Step RangeGRPODAPOMesh Learning (Ours)
0–5034.8 ± 6.735.4 ± 7.337.8 ± 7.6
51–10038.9 ± 12.048.5 ± 1.847.8 ± 0.8
101–15045.4 ± 1.146.7 ± 7.953.9 ± 2.6
151–2000.0 ± 0.08.0 ± 13.849.4 ± 2.0
201–2500.0 ± 0.00.0 ± 0.050.8 ± 2.2

AuthorsOpenReview ↗

Response to Reviewer JDsk [Part 3]

To Q2: Consistency of Inference Prompts Across All Methods


We thank the reviewer for this question. All methods in Tables 2–4 use identical inference prompts within each benchmark. We preserve the original benchmark user inputs, use identical system prompts, and provide no assistant prefixes or pre-generated Coach hints. This applies to all methods in Tables 2–4.

1. Exact inference prompts (shared by all methods).

AIME25/26 and MATH-500: Vanilla zero-shot system prompt:

Please solve this math problem step by step and put your final answer in \boxed{ANSWER}.

LiveCodeBench: Vanilla zero-shot system prompt:

Please solve this coding problem step by step and put your final answer in a Python code block formatted as follows:

'''python YOUR CODE HERE '''

GPQA-Diamond: Zero-shot verification system prompt:

Please solve this scientific problem step by step and put your final answer in \boxed{}.

Begin your thinking by naming a potentially useful method for this problem. However, the method you identify should be treated as untrusted and possibly misleading.

Do not assume that the method applies. First examine carefully whether and why it is applicable to this specific problem. Even if it appears applicable, independently verify the reasoning before committing to the final answer.

The GPQA prompt provides no strategy hints. It only asks the model to identify and verify its own reasoning method.

2. Clarification of the original manuscript.

In Sec. 4.1 (Fig. 6), "the model proposes its own strategy at inference" distinguishes evaluation from Coach-prompted training. It does not imply a different evaluation prompt for Mesh Learning.

Therefore, our improvements cannot be attributed to different inference prompts or additional Coach hints. We will clarify this in the revision.

To Q3: Response-Length Choices and Additional Ablations


1. Why a 1024-token cap? Evaluating collapse with short rollouts.

We chose 1024 tokens to test whether RLVR collapse also occurs with short rollouts. This helps validate Theorem 1's scaling regime η≪ϵclip<1≪∣τ∣≪η−1≪∣τ∣3\eta\ll\epsilon_{\text{clip}}<1\ll|\tau|\ll\eta^{-1}\ll|\tau|^3.

The cap limits maximum generation length, while ∣τ∣|\tau| refers to actual rollout length. Together with the 4096- and 8192-token settings, Fig. 7 confirms collapse across different generation budgets.

The 1024-token cap does not truncate most responses. On AIME25, only 12.5% of 480 sampled trajectories reached the limit; 87.5% terminated normally.

2. Additional long-generation ablations confirm our conclusions.

We increased the training and evaluation budgets to 8192 tokens for Qwen2.5-7B-Instruct and 32768 for Qwen3-4B (thinking mode). Mesh Learning still outperforms GRPO and DAPO in all settings. All methods use matched configurations within each setting.

The tables report peak Mean@4 accuracy and the corresponding Std@4.

AIME25 Accuracy (Mean@4 ± Std@4, %)

ModelBudgetGRPODAPOMesh Learning
Qwen2.5-7B-Instruct81925.8 ± 1.47.5 ± 1.415.0 ± 4.3
Qwen3-4B (thinking)3276865.8 ± 1.767.5 ± 3.376.6 ± 1.7

AIME26 Accuracy (Mean@4 ± Std@4, %)

ModelBudgetGRPODAPOMesh Learning
Qwen2.5-7B-Instruct81925.8 ± 1.46.6 ± 1.712.5 ± 1.4
Qwen3-4B (thinking)3276865.8 ± 1.769.1 ± 3.173.3 ± 3.1

At the larger budget, our base-model evaluation of Qwen3-4B (thinking mode) matches its officially reported AIME25 accuracy of 65.6% (Qwen3 Technical Report).

For Qwen2.5-7B-Instruct, an eightfold larger budget does not consistently improve accuracy. Compared with Table 2, GRPO drops from 13.3% to 5.8% on AIME25 and from 9.2% to 5.8% on AIME26. DAPO changes from 6.7% to 7.5% and 8.3% to 6.6%, respectively. Mesh Learning maintains similar accuracy (16.7% to 15.0%; 13.3% to 12.5%) and retains its advantage.

For Qwen3-4B, longer generations substantially improve accuracy, but Mesh Learning still performs best. GRPO and DAPO also exhibit late-stage collapse under the extended budget, consistent with Theorem 1.

Overall, Mesh Learning remains effective across short and long generation budgets. We will include these experiments in the revised main paper.

Reviewer_6rQcOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies the late-stage performance collapse that occurs during reinforcement learning with verifiable rewards (RLVR) for large language models. The authors argue that this phenomenon stems from competition among different reasoning strategies during optimization, which causes the policy probability to gradually concentrate and reduces the effective strategy capacity. To explain this mechanism, the paper defines reasoning strategies based on gradient coupling relationships among trajectories, and proposes a unified theoretical framework analyzing the tension between strategy concentration and the strategy capacity required to maintain task accuracy. Meanwhile, the authors propose the Mirrored Entanglement Index (MEI) as an online early-warning indicator of strategy collapse. To mitigate this problem, the authors propose Mesh Learning, which combines Coach Prompting and Strategy-Balancing Regularization to explicitly introduce multiple reasoning strategies during training and balance their relative growth rates. The experiments cover Qwen and Phi models, as well as benchmarks such as AIME, MATH-500, GPQA, and LiveCodeBench. The results show that this method can improve reasoning accuracy and, in some experiments, effectively avoid late-stage performance collapse.

Critical strengths
  • The paper attempts to theoretically explain the performance collapse of RLVR. The paper connects the late-stage performance degradation of RLVR with reasoning strategy capacity, proposes a definition of strategies based on optimization dynamics, and attempts to explain the strategy concentration phenomenon through theoretical analysis. MEI provides a potentially practical tool for monitoring strategy collapse.

  • The method design is reasonable, and the experimental results are fairly convincing. The paper achieves consistent performance improvements across multiple model families and mathematical, scientific, and code reasoning tasks, and supports the method's effectiveness through training dynamics analyses and partial ablation studies. These results indicate that the method has practical application value, rather than being applicable only to a single model or task.

Critical weaknesses
  • Doubts remain regarding the rigor of the core theoretical results and their interconnections. Theorem 1 claims that mainstream RLVR algorithms lead to the concentration of policy probability, but its proof relies on conditions such as the existence of non-degenerate effective updates among strategies and the fitness of strategies not being completely identical. These key conditions are not sufficiently clarified in the main theorem, leaving the scope of applicability of the conclusion in question. In addition, it remains unclear whether the global strategy capacity lower bound given by Theorem 2 is sufficient to prove that multiple reasoning strategies must be preserved in order to maintain high accuracy. Since the strategy sets corresponding to different questions do not overlap, this lower bound may in some cases be weaker than the trivial lower bound obtained by preserving at least one strategy per question. Therefore, whether Theorems 1 and 2 genuinely constitute the contradiction claimed by the authors requires further justification. This directly affects the paper's most central theoretical contribution.
Questions for authors

1. On the applicability conditions of Theorem 1. Does Theorem 1 implicitly require different strategies to have non-zero and not completely identical effective updates? When multiple strategies have the same reward, the within-group advantage is zero, or the effective gradients cancel out, does the theorem still hold? Please clearly state whether these cases are excluded by the theorem's assumptions, and provide the corresponding theoretical justification.

2. On the connection between Theorem 2 and strategy collapse. Since the strategy sets corresponding to different queries do not overlap, and each query can retain at least one usable strategy, how do the authors ensure that the derived global strategy capacity lower bound is non-trivial? In particular, how does this lower bound rule out the case where each query retains only one strategy, and how does it form a strict contradiction with Theorem 1?

5 comments
AuthorsOpenReview ↗

Response to Reviewer 6rQc [Q1 Part 1]

We sincerely thank Reviewer 6rQc for the time and effort devoted to carefully examining our theoretical analysis. Below, we address the reviewer's two questions in detail.

Note: We have uploaded a slightly revised manuscript with two minor updates: (1) adding an actual model-generated trajectory as an illustrative example, and (2) refining the mathematical rigor of one lemma. The main theoretical and experimental results remain unchanged. Both updates are directly relevant to our response below. Please refer to the latest PDF when assessing our responses.


To Q1: Applicability and Non-Degeneracy Conditions of Theorem 1

Theorem 1 allows occasional zero-advantage groups and zero sampled updates; neither implies degeneracy of the population dynamics. Our analysis adopts a standard non-orthogonality condition, supported by the empirical gradient geometry in Fig. 2. Under this condition, our derivation rules out persistent degeneracy of the effective population drift. Moreover, equal strategy fitness does not imply identical dynamics, as sampling noise can destabilize their balance.

1. The non-degeneracy condition.

Theorem 1 relies on a non-degeneracy condition that is already used in our original proof. We will make this condition explicit in the theorem statement.

Specifically, Appendix A.2.3 (Lemma 3, Eq. (87)) assumes local non-orthogonality between trajectory scores and parameter updates:

\ge\kappa|U_i||\Delta\theta_k|,\qquad\kappa>0,$$ for the nonzero scores and updates considered. **Such conditions are common in optimization** ([1] Gilbert and Nocedal, 1992; [2] Bottou et al., 2018; [3] Huo et al., 2018). **Our experiments also support this geometric assumption.** For single-rollout updates, Sec. 2.1 gives $U_i^\top\Delta\theta_k=\eta A_jK_{ij}$. Fig. 2 shows that both within- and across-strategy couplings $K_{ij}$ are typically nonzero and substantial, apart from the light-shaded tails. This provides empirical support for nontrivial gradient interactions. ### **2. Occasional zero updates do not invalidate our analysis.** **A rollout group can have zero advantage without making the overall RLVR optimization ineffective.** Our proof already accounts for all-correct and all-wrong groups through the stochastic update decomposition. Under independent sampling, unnormalized centered advantages, and no clipping, Appendix A.2.1, Eq. (24), gives $$\mathbb E[A_{j,k}\mid\tau_j,Q',\mathcal F_k] =\frac{G-1}{G}\bigl(r(\tau_j)-p_k(Q')\bigr),$$ which averages over all possible sampled groups, including all-correct and all-wrong groups. More importantly, Eqs. (23)–(30) already separate stochastic parameter updates into a conditional population drift and zero-mean sampling noise. **Therefore, occasional zero or identical sampled updates do not imply that the population drift vanishes.** These fluctuations are already included in our analysis, and the Azuma–Hoeffding argument applies under the proof's non-degeneracy conditions. ### **3. How do parameter updates change strategy probabilities?** **The key to strategy competition is whether different strategies gain or lose probability mass at different rates.** To examine this, we rewrite the strategy-level dynamics already derived in Eqs. (191), (195), and (197). To first order, $$\begin{aligned}\bar U_\alpha&=\nabla_\theta\log\nu_\alpha=\sum_{i\in S_\alpha}q_{i\mid\alpha}U_i\\\\ \Delta\log\nu_\alpha&=\underbrace{\bar U_\alpha^\top}_{\text{strategy score}}\Delta\theta_k\\\\ &=\eta\underbrace{f_{\alpha,k}}_{\text{fitness}}+\frac{\overbrace{\xi_{\alpha,k}}^{\text{noise}}}{\nu_\alpha},\qquad\mathbb E_k[\xi_{\alpha,k}]=0\end{aligned}$$ This expression directly connects parameter updates with changes in strategy log-probabilities. Each strategy has its own mean score $\bar U_\alpha$, which determines how its probability changes under the same parameter update. This also allows us to examine whether all strategies can receive identical probability changes. ----- [1] Gilbert, Jean Charles, and Jorge Nocedal. "Global convergence properties of conjugate gradient methods for optimization." *SIAM Journal on optimization* 2.1 (1992): 21-42. [2] Bottou, Léon, Frank E. Curtis, and Jorge Nocedal. "Optimization methods for large-scale machine learning." *SIAM review* 60.2 (2018): 223-311. [3] Huo, Zhouyuan, Bin Gu, and Heng Huang. "Training neural networks using features replay." *Advances in Neural Information Processing Systems* 31 (2018).
AuthorsOpenReview ↗

Response to Reviewer 6rQc [Q1 Part 2]

4. Why can persistent identical strategy updates be excluded?

If every strategy receives the same change in log-probability, that change must be zero. Under our non-degeneracy conditions, persistent zero changes are excluded, so strategies cannot all maintain identical growth rates.

First, Eq. (195) shows that each strategy's change in log-probability is a weighted average of its trajectories' changes:

=\sum_{j\in S_\alpha}q_{j\mid\alpha}U_j^\top\Delta\theta_k.$$ By Eq. (223), $\sum_\alpha\nu_\alpha\bar U_\alpha=0$. If every strategy has the same change $c$, then $$c=\sum_\alpha\nu_\alpha\bar U_\alpha^\top\Delta\theta_k=0.$$ **Thus, identical strategy-level probability changes can only occur when all these changes are zero.** We now examine this fully degenerate case. Under the first-order, frozen-coefficient analysis, the update–potential relation (Eqs. (195), (212)–(215)), the drift bound (Eq. (233)), and the error bounds (Eqs. (217), (219)–(220)) yield $$\begin{aligned} \mathbb E\left[|\Delta\theta_k|^2\mid\mathcal F_k\right] &\ge\bigl|\mathbb E[\Delta\theta_k\mid\mathcal F_k]\bigr|^2\ &\ge\eta^2|g_k|^2-\mathcal O(\eta^2\epsilon) -\mathcal O_{\mathbb P}\left(\eta^2\bigl[|\mathcal D|^{-1/2}+|\mathcal D'|^{-1/2}\bigr]\right). \end{aligned}$$ Lemma 14 explicitly constructs a strategy with a **distinct advantage coefficient**, thereby establishing $|g_k|^2>0$ almost surely. When $\epsilon$ is sufficiently small and the datasets are sufficiently large, the error terms remain below this positive signal, giving a nonzero mean update. Our experiments also show nonzero per-step parameter updates, with $|\Delta\theta_k|\in[0.1,0.3]$. **The non-orthogonality condition further connects nonzero parameter updates to nonzero changes in strategy probabilities.** Eqs. (68)–(71) relate the relative changing rates of strategy and trajectory probabilities, $\omega_\nu$ and $\omega_\pi$. Under $\epsilon\ll\kappa$ and on a common response scale, Eqs. (17) and (73) give $$|\bar U_\alpha^\top\mathbb E_k[\Delta\theta_k]| \approx \omega_\nu \approx \omega_\pi \approx |U_i^\top\mathbb E_k[\Delta\theta_k]|,\qquad i\in S_\alpha.$$ Together with the non-degeneracy condition in Part 1, these results rule out persistent all-zero or all-identical strategy probability changes within the analyzed regime. **This establishes the effective competition between strategies required by our concentration analysis.** ### **5. Equal fitness does not guarantee stable coexistence.** **Even if two strategies have identical fitness, their probabilities need not remain balanced.** Sampling noise can break the balance and increase the difference between their probability masses. To illustrate this, consider an extreme case with two strategies $S_1,S_2$. They have equal maximal advantage and fitness, $a_1=a_2=a$ and $f_1=f_2=f$, and dominate nearly all probability mass in late-stage training (Appendix A.2.4). Suppose $\nu_1\approx\nu_2\approx1/2$, while nontrivial failure rates remain. By Eq. (197), $$\Delta\nu_{i,k}=\eta f\nu_{i,k}+\xi_{i,k},\qquad i=1,2.$$ Since $\sum_\alpha\nu_\alpha f_\alpha=0$ (Eq. (164)) and probability is conserved, we have $\sum_\alpha\xi_{\alpha,k}=0$. With other strategies nearly absent, we approximate $\xi_{1,k}+\xi_{2,k}=0$. Set $s_k=\nu_{1,k}+\nu_{2,k}$ and $r_k=(\nu_{1,k}-\nu_{2,k})/s_k$. The zero-mean noise then yields $$\mathbb E_k[r_{k+1}^2-r_k^2] =\frac{\mathbb E_k[(\xi_{1,k}-\xi_{2,k})^2]}{(1+\eta f)^2s_k^2}>0.$$ **Therefore, even at equal fitness, sampling noise increases the expected squared difference between strategy probabilities.** This can destabilize balanced coexistence and contribute to further concentration. **Our experiments provide a concrete illustration.** In Appendix E (pp. 61–63,66-67), Qwen2.5-7B-Instruct initially exhibits two stable strategies on the same query, with similar frequencies, accuracies, and no apparent difference in difficulty. Yet one strategy eventually dominates. Two independent runs converge to different winning strategies, consistent with this noise-driven explanation.
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Response to Reviewer 6rQc [Q2 Part 1]

To Q2: Non-Triviality of the Strategy Capacity Lower Bound and Its Connection to Collapse


Short answer: the two results can be incompatible in a specific accuracy range (Pc,1)(P_c,1), and our training results support this range.

1. How do Theorems 1 and 2 connect?

The reviewer's one-strategy-per-query scenario is the limiting case of strategy concentration. The connection between Theorems 1 and 2 is easiest to see through the entropy-based effective strategy capacity, Seff,k=2H(S^ϵ,k)S_{\mathrm{eff},k}=2^{H(\widehat S_{\epsilon,k})}. With uniformly sampled queries and disjoint query-specific strategy sets, the entropy decomposition in Eq. (313) gives

Seff,k=N⋅2H(S^ϵ,k∣Q),S_{\mathrm{eff},k}=N\cdot 2^{H(\widehat S_{\epsilon,k}\mid Q)},

where NN is the number of evaluation queries.

When each query retains exactly one strategy, its conditional entropy is zero, giving Seff,k=NS_{\mathrm{eff},k}=N. The near-concentration established by Theorem 1 similarly drives effective capacity toward NN, with a small residual entropy contribution. Theorem 2's entropy bound (Eqs. (305), (313)–(316)) also gives a lower bound on effective capacity.

Within their common validity window, the two results can be directly compared: if the required capacity exceeds NN, exact one-strategy-per-query collapse is incompatible with the lower bound; for near-collapse, the bound must exceed N⋅2H(S^ϵ,k∣Q)N\cdot 2^{H(\widehat S_{\epsilon,k}\mid Q)}, including residual entropy.

2. When does strategy concentration become incompatible with high accuracy?

Not every model or task must experience collapse. The conflict only arises when the required capacity exceeds the capacity remaining after strategy concentration.

Theorem 2 identifies when this conflict can occur. For a fixed model and dataset, Theorem 2 (p. 4, Eq. (4)) gives

∣S^ϵ,k∣≥CNPacc,k,|\widehat{\mathcal S}_{\epsilon,k}| \ge C N^{P_{acc,k}},

where CC is the lower-bound coefficient. Eq. (316) gives

Ctheory=2ρmϵ(1+ρ)2,2−O(η2∣τ∣2)N−γ.C_{\mathrm{theory}}=\frac{2\rho m_\epsilon}{(1+\rho)^2}\\,2^{-\mathcal O(\eta^2|\tau|^2)}N^{-\gamma}.

This theoretical bound is conservative. The proof uses a cross-entropy relaxation (Eq. (302)) and Fano's inequality (Eq. (312)). Both can introduce slack. Eq. (317) provides an approximation in the saturated regime. Fig. 3 also shows that measured strategy capacities exceed the theoretical bound. We therefore estimate an empirical coefficient from training data. This provides additional evidence, not a tighter theoretical guarantee.

We can now compare the lower bound with NN. For any theoretically valid lower-bound coefficient CC, the required capacity exceeds NN when

P_{acc,k}>P_c=1-\frac{\log C}{\log N}. }$$ **This is the condition for a capacity conflict against this lower bound.** Above $P_c$, further concentration toward $N$ becomes incompatible with maintaining the achieved accuracy. Near-concentration requires accounting for residual strategy entropy. If $P_c\ge1$, the bound gives no such conflict at attainable accuracies.
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Paper summary

As I understand it, the core idea is quite simple: generate different strategy hints for the same question, sample rollouts under each hint, and optimize them together using GRPO with an additional balancing loss. There are already many related works on hint-guided RL, diverse exploration, and preventing diversity collapse. I don't see a particularly strong methodological contribution here, and the paper does not clearly explain how it differs from existing approaches.

Critical strengths

The experiments cover multiple models and benchmarks, showing consistent improvements over several RLVR baselines, especially on Pass@k.

Critical weaknesses
  1. Limited Novelty: The core idea is to use different strategy hints for grouped rollouts and jointly optimize them with GRPO. Similar ideas have been widely explored in prior work.

  2. Overly Complicated Presentation: The paper is 84 pages long, with dozens of pages of mathematical proofs. I find this excessive for such a simple method.

Questions for authors

N/A

2 comments
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Response to Reviewer ceC2

We thank the reviewer for the feedback and for acknowledging the consistent improvements across multiple models and benchmarks. We would like to clarify two key concerns regarding the novelty of our contributions and the length of the appendices, which we believe may stem from an incomplete characterization of the paper's theoretical focus.


To Q1: Novelty beyond strategy prompting and GRPO tuning.

Our Learning Theory submission explains RLVR's late-stage accuracy cliff, beyond reduced diversity. Assessing novelty primarily through strategy hints and a GRPO balancing loss overlooks six contributions centered on our theoretical framework:

1. Strategy definition (Sec. 2). We define strategies through trajectory-level gradient coupling, making their optimization dynamics mathematically tractable; Sec. 2.2 empirically examines their correspondence to semantic solution methods, showing that our definition has both theoretical rigor and experimental relevance.

2. Concentration mechanism (Theorem 1). Under the stated assumptions and scale conditions in real training configurations η≪ϵclip<1≪∣τ∣≪η−1≪∣τ∣3\eta\ll\epsilon_{\text{clip}}<1\ll|\tau|\ll\eta^{-1}\ll|\tau|^3, three typical RLVR recipes, GRPO, DAPO, and GSPO, concentrate probability mass onto one strategy with high probability over a specified finite training window.

3. Strategy-capacity scaling law (Theorem 2). We quantify how much strategy capacity is needed to sustain a given accuracy. Together with Theorem 1, this explains why losing strategies can cause accuracy to collapse, connecting reduced diversity to actual performance failure.

4. Early-warning indicator (Sec. 3.3; Appendix B). We turn our collapse theory into MEI, a lightweight signal that warns of collapse while accuracy still appears healthy. It provides advance warning before the observed accuracy cliffs across the training settings. (Figs. 4 and 7)

5. Regularization limits (Theorem 3). Sufficiently large effective reward gaps relative to fixed KL/JS penalty strength drive the optimal strategy distribution arbitrarily close to one-hot. Fixed-strength divergence penalties therefore cannot universally prevent concentration.

6. Theory-guided prevention (Sec. 4). Mesh Learning is designed to prevent collapse by exposing and balancing multiple strategies throughout training. Strategy hints are only one component: our ablations (Table 2) show that hints alone yield little or no improvement, while full Mesh Learning consistently performs better. The key is preserving the exposed strategies through balanced optimization, not simply providing hints.

Sec. 6 discusses related work. We welcome scrutiny of our assumptions and derivations, and ask which of these theoretical, diagnostic, or methodological contributions are already established by specific prior work.

To Q2: What the appendices contain.

The current manuscript has 9 main-text pages, 3 reference pages, and 74 appendix pages, organized as follows:

PagesContentLength
13-40Framework and Theorem 1 proof28
41-44Theorem 2 proof4
45-48MEI properties4
49-52Theorem 3 proof4
53-56Mesh Learning analysis4
57-60Experimental protocols/configurations4
61-86Representative trajectory case studies26

The mathematical justification of Mesh Learning occupies only 4 pages; 40 pages develop the collapse theory, 4 pages document experimental configurations, and 26 pages provide actual model trajectories from training experiments. The simplicity of the method should not be confused with the complexity of the problem it addresses.

We welcome specific criticisms of unnecessary derivations, redundant proofs, or presentation issues, but the total page count alone does not establish that the paper is unnecessarily complicated.


We respectfully ask the reviewer to distinguish the novelty of individual algorithmic components from that of our theoretical framework, and to identify which of our six contributions have already been established in prior work. As clarified in Q2, the extensive appendices are not unnecessary elaborations of a simple method; each section serves a specific purpose, providing theoretical proofs, diagnostic analysis, reproducibility details, or qualitative evidence. We hope these explanations address the reviewer's concerns and encourage a reconsideration of the overall assessment.

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Gentle Follow-up on Our Author Response

Dear Reviewer ceC2,

We have provided a detailed response clarifying our six theoretical and methodological contributions, as well as the purpose of the appendices.

We would appreciate it if you could carefully consider these clarifications and reconsider your assessment of our paper.

Comments on the paper

1 comment
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Rebuttal Summary

We sincerely thank all reviewers for their feedback. During the rebuttal period, we directly addressed every theoretical and experimental question with detailed explanations, additional evidence, and manuscript revisions. These include theoretical assumptions, empirical collapse predictions, training-stage analyses, long-generation experiments, and evaluation protocols.

Reviewer 6rQc

We clarified Theorem 1's non-orthogonality condition and addressed all edge cases raised by the reviewer. Our existing 15 lemmas and 278 equations, together with simple algebraic arguments in our rebuttal and extensive empirical evidence in Appendix E, show that occasional or persistent zero/identical updates are either covered by our theoretical analysis or ruled out under realistic conditions. We incorporated the necessary clarifications into the latest manuscript.

We established an explicit connection between Theorems 1 and 2, directly addressing the one-strategy-per-query concern. We further derived and calibrated critical accuracy thresholds of 59.5% (Qwen2.5-7B-Instruct, MATH-500) and 27.1% (Qwen3-4B, AIME25), above which collapse may occur. All 20 observed collapse cases in Table 2 satisfy these thresholds. Thus, the concern fits our theoretical framework and yields an additional experimentally supported prediction.

Discussion status: The reviewer acknowledged that our detailed explanations helped him better understand the theorem, but maintained concerns about methodological novelty rather than reiterating his original theoretical objections. We asked whether any specific theoretical concerns remained, but received no further clarification.

Reviewer JDsk

We addressed all four concerns about statistical reliability, inference fairness, generation length, and strategy grouping through experiments and revisions.

1. We clarified checkpoint selection and added Std@4 to Tables 2–4. Each method uses its best checkpoint per benchmark. Training-stage statistics cover 4 benchmarks and 11 model–benchmark settings. Mesh Learning ranks first in 53 of 59 phases (3 ties); 33 of 40 baseline runs drop to 0% accuracy, versus 0 of 11 Mesh runs. Improvements thus persist throughout training rather than arising from checkpoint selection.

2. We clarified in both our rebuttal and the revised manuscript (Sec. 5.1) that all methods use identical system prompts within each benchmark. Therefore, the reviewer's concern about inconsistent inference prompts does not apply to our experiments.

3. The 1024-token limit was chosen to test the theory under short-generation constraints. At 32768 tokens, Mesh still achieved 76.6% on AIME25 and 73.3% on AIME26, surpassing the strongest baselines by 9.1 and 4.2 pps.

4. Strategy grouping requires no online kernel classification. Experiments across three model families and four datasets show 87–97% strategy adherence on mathematical tasks, supporting its practical reliability.

Discussion status: No further concerns or clarification requests have been posted.

Reviewer ceC2

Our Learning Theory submission's primary novelty is its theoretical framework, not merely strategy prompting or another GRPO loss. We contribute six theory contributions: a gradient-coupling-based strategy definition, strategy concentration, a capacity lower bound explaining accuracy collapse, the MEI early-warning indicator, limits of fixed KL/JS regularization, and theory-guided Mesh Learning.

The extensive appendices substantiate these theoretical contributions rather than unnecessarily complicating a simple method. 40 of 74 appendix pages develop the theoretical framework. The complexity of characterizing RLVR collapse should not be confused with the simplicity of its prevention.

Discussion status: No further concerns or clarification requests have been posted.

Overall Conclusion

All specific reviewer questions received theoretical or experimental responses. The revised manuscript and rebuttal provide explicit assumptions, calibrated thresholds, training-stage statistics, Std@4, identical inference protocols, long-generation ablations, and strategy-adherence measurements.

Our work is not merely a method for preventing strategy collapse, but a coherent framework that explains its underlying mechanism, predicts its onset, and provides a theory-guided solution. We hope the reviewers and Area Chair will evaluate these interconnected theoretical and empirical contributions as a whole, rather than focusing on the novelty of individual algorithmic components, in the spirit of ICLR's commitment to rigorous and fair scientific evaluation.

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

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