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Under review as a conference paper at ICLR 2027

Timeout Is Not a Negative Label: Learning from Budget-Censored Verification

Abstract

A training timeout can leave a program's outcome unknown at the verification limit that defines task success. We study randomized verification allocation that preserves the policy gradient of this reference objective. Building on inverse weighting and randomized truncation, we derive the allocation criterion for the smooth improvement bound of an ordinary policy minibatch. Finite batching adds a squared-mean-gradient term to the usual cost–second-moment product, which can change the optimal allocation. Under an unknown trace law and a fixed observation kernel, universally unbiased conditional allocation feedback requires two independent records for the usual product and, in general, three for the finite-batch criterion. Distinct-record estimators attain these orders using only censored observations. In a high-signal control, the optimal verification probability changes from one to approximately , reducing the finite-batch objective by . Censored feedback learns this allocation, although a plug-in estimator is more efficient in the stationary control. A separate executed-program study requires delayed verification for optimal program choice on half the held-out prompts. Negative timeout labels exclude those choices. Checkpoint analysis and exact update moments clarify when allocation improvements have an efficiency interpretation. These results characterize observable allocation feedback without implying a general training-speed advantage.

Primary area:
reinforcement learning
Keywords:
reinforcement learning, verifiable rewards, budget-censored verification, policy gradients, unbiased estimation, adaptive computation allocation, inverse probability weighting, randomized truncation, minibatch optimization, learning theory

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

The paper studies policy learning when program verification is deliberately stopped early to save computation, so some outcomes are censored before the reference verification limit. Rather than treating a training-time timeout as failure, the method randomizes verification depth and uses inverse weighting to preserve the reference objective. The paper derives the computation-allocation criterion relevant to finite minibatches, showing that it can differ from the standard cost-versus-second-moment objective. It further characterizes how many independent censored records are necessary to obtain universally unbiased allocation feedback under the stated observation model. Experiments include a controlled high-signal setting in which the preferred verification allocation changes substantially and a constructed program-selection study in which slower candidates are required for optimal choices on part of the test set.

Critical strengths

The paper identifies a subtle but important objective mismatch. A timeout caused by a reduced training-time verification budget does not reveal the same information as failure at the task’s reference budget. The paper makes this distinction precise and provides an unbiased correction that preserves the intended learning objective under adaptive randomized verification.

The finite-batch analysis and feedback-order characterization are technically substantive. The result that finite batching changes the relevant allocation objective, together with the two-record versus three-record distinction under the unknown-law model, goes beyond applying standard inverse weighting. The experimental controls are also well aligned with these theoretical mechanisms.

Critical weaknesses

The empirical evidence does not yet establish a meaningful end-to-end training-efficiency improvement in realistic code-generation settings. The authors explicitly frame the experiments as mechanism studies and caution that the results do not imply a general training-speed advantage. This appropriate caveat also limits the practical impact that can currently be inferred from the paper.

The theoretically clean unbiased-feedback constructions may be statistically expensive in the regime that motivates the work. Requiring multiple independent records for allocation feedback, together with potentially large inverse-probability corrections for rarely verified endpoints, can offset computation savings through higher variance. Indeed, the paper reports that a plug-in estimator can be more efficient in its stationary control, making the practical choice between exact unbiasedness and historical estimation important.

Questions for authors

Can you report end-to-end wall-clock or verifier-compute learning curves comparing full verification, corrected fixed schedules, plug-in adaptation, and the unbiased adaptive method, rather than only the allocation criterion or final program-selection behavior?

In what empirical regimes does the variance introduced by rare verification and inverse weighting overwhelm the compute savings? Is there a practical diagnostic for identifying this regime before training?

Do the conclusions continue to hold for natural model-generated code and learned representations, rather than the constructed program family used to isolate the mechanism?

2 comments

Thank you for identifying the finite-batch feedback contribution. We agree that unbiased allocation feedback need not be statistically most efficient and that the studies do not establish language-model training acceleration.

  1. Learning curves and complete accounting. Figure 1 reports held-out success throughout the slow-optimal study for the requested methods. Its axis is logical work, not elapsed time.

The addendum reconstructs time-based curves from stored snapshots of all seven methods in the separate CPU-budgeted experiment (Appendix M.7, eight seeds per method), without retraining. It uses the latest saved policy at each time, not continuous monitoring. The two-second endpoint uses the original final policies, with batch-stopping overshoot below 0.00064 seconds.

For ordinary mean updates, endpoint means are 81.63% for full verification, 78.83% for fixed correction, 73.44% for plug-in, 83.00% for paired-CMCM, and 83.05% for batch-aware allocation. The batch-aware/full paired difference is 1.42 points [0.09, 2.74], whereas batch-aware/fixed is 4.22 [-1.80, 10.25] and batch-aware/paired is 0.05 [-0.17, 0.27]. Intervals are unadjusted. These data do not establish an incremental training advantage from the triple term. The reward-only comparator, also retained in the curves, has the highest mean, 84.67%.

The timer includes sampling, source construction, compilation, verification, policy updates, allocator updates, and solver calls. It excludes common initialization, development search, reference-bank construction, and final evaluation. It measures process CPU, not accelerator wall-clock latency. The older four-prompt CPU-negative result remains in Appendix N. Neither experiment supports a general runtime claim.

  1. When does variance outweigh saved computation? For a common one-checkpoint survival qq, deterministic verification time dd, overhead c0c_0, and a=E∣Z∣2a=E|Z|^2, Proposition 3 gives C=c0+dq,M=a/q,q=clip⁡[ϵ,1]κ/ξ,C=c_0+dq,\quad M=a/q,\quad q^=\operatorname{clip}_{[\epsilon,1]}\sqrt{\kappa/\xi}, where κ=c0/d\kappa=c_0/d and ξ=(n−1)∣γ∣2/a\xi=(n-1)|\gamma|^2/a. At ξ=0\xi=0, set q=1q^=1. Thus full verification minimizes the finite-batch criterion when ξ≤κ\xi\le\kappa: weak gradient signal or large non-verification overhead removes the predicted benefit of thinning in this model. The policy-gradient second moment grows as 1/q1/q, while the generic allocation-feedback bound can grow as ϵ−3\epsilon^{-3}. This is precisely the tension noted in the review.

A practical diagnostic is a separately charged, independent full-budget pilot. Freeze the policy and estimate candidate schedules' cost, corrected second moments, and squared mean gradient. Compare Φn(u)/Φn(0)\Phi_n(u)/\Phi_n(0) with uncertainty, including generation and allocation overhead in measured costs. Cross-record inner products estimate the squared mean without the squared-sample-mean bias. A point estimate below one is insufficient. Rare endpoints, second moments dominated by a few weighted records, and wide uncertainty favor full verification or a higher floor. Recheck as the policy changes. This is a proposed operational diagnostic, not a validated selection guarantee or a certificate of final accuracy.

  1. Exact feedback versus historical estimation. Theorem 5 does not assert that direct feedback beats plug-in learning. At 12,000 records in the stationary control, triple feedback has 0.57% oracle excess versus 0.03% for plug-in. Historical averaging can be preferable when the law is stable. The distinction is that direct feedback remains conditionally unbiased at the current policy. For an existing batch of at least three independent records, it reuses those records rather than requiring three extra batches. Per-record policy scores can still be expensive. Adaptive unbiased-truncation research [1] likewise treats estimation costs as a design issue.

  2. Natural code and learned representations. Objective preservation extends to such policies only under the stated randomization and regularity assumptions. The grammar does not enter the identity, but empirical timeout prevalence, score computation, parallel scheduling, and policy drift do enter practical efficiency. We have not tested natural model-generated code or learned representations. Contemporary rollout scheduling [2] addresses a related selection/reuse decision, not evidence that our censoring correction accelerates those systems. Our conclusion remains the feedback classification, not general practical acceleration.

[1] Zheng, Pan, and Wang. Optimal Distributions for Randomized Unbiased Estimators with an Infinite Horizon and an Adaptive Algorithm. IMA Journal of Numerical Analysis, 2026.

[2] Lu et al. Contextual Rollout Bandits for Reinforcement Learning with Verifiable Rewards. ICML, 2026.

Thank you for identifying the finite-batch criterion and record-order characterization as substantive contributions. We have incorporated the requested computation and sensitivity analyses into the manuscript, with changes in blue. The principal additions are Section 7.3 and Appendix O, while Section 8 now gives the operational interpretation of the allocation regimes.

  1. Complete CPU learning curves and accounting. Appendix O.3, Figure 11, and Table 25 now report the saved-policy learning curves and paired endpoint comparisons for all seven allocation rules in the CPU-matched checkpoint study, with eight seeds per method. The curves evaluate the latest stored policy at or before each displayed time. They use the original CPU records, not new timing measurements or replay timings.

At the nominal two-second target, mean held-out success is 81.63% for full verification, 78.83% for fixed correction, 73.44% for plug-in, 83.00% for paired-CM, and 83.05% for batch-aware allocation. The batch-aware/full paired difference is +1.42 points [0.09, 2.74]. The corresponding fixed and paired-CM differences are +4.22 [-1.80, 10.25] and +0.05 [-0.17, 0.27]. Reward-only, also included, has the largest observed mean, 84.67%. The intervals are unadjusted.

The clock includes sampling, program construction, compilation, verification, policy-score computation, policy and allocation updates, solver calls, and in-loop bookkeeping. Common initialization, development search, reference-bank construction, and final evaluation remain outside the clock. Endpoint policies retain the original batch-stopping overshoot, below 0.00064 seconds. Process CPU is distinguished from wall-clock latency and from the logical-work theorem. Figure 1 and Table 2 remain the separate slow-optimal program study, and the four-prompt CPU-negative control remains in Appendix N.

  1. When does rare-verification variance outweigh the saving? Section 8 now highlights the boundary from Proposition 3. With one checkpoint, common survival qq, deterministic verification cost dd, overhead c0c_0, and a=E∣Z∣2a=E|Z|^2, define κ=c0/d\kappa=c_0/d and ξ=(n−1)∣γ∣2/a\xi=(n-1)|\gamma|^2/a. Full verification minimizes the finite-batch criterion when ξ≤κ\xi\le\kappa. Above that boundary, the optimum is κ/ξ\sqrt{\kappa/\xi} until the floor binds. Thus weak mean-gradient signal or large per-program overhead can favor full verification. The corrected policy second moment grows as 1/q1/q, and the generic allocation-feedback bound can grow as ϵ−3\epsilon^{-3}.

Appendix O.4 describes an optional, separately charged full-budget pilot at a frozen policy. It estimates candidate schedules' expected costs, corrected second moments, and squared mean gradient, using distinct-record inner products for the last quantity. Comparing allocation criteria with uncertainty, including generation and allocation overhead, is more informative than comparing raw verifier costs. A few weighted endpoints dominating the second moment or wide uncertainty favor a higher floor or a simpler corrected schedule. This is a proposed diagnostic for method selection, not an experimentally validated selection guarantee. The allocation algorithm itself needs no complete pilot traces.

  1. Sensitivity and the exact-feedback/plug-in tradeoff. Appendix O.1 adds the full 96-run floor/step sweep. With the development-selected policy step fixed, mean success ranges from 78.20% to 80.20% across twelve settings. The default allocation step gives identical trajectories across the tested floors, while the largest step makes the floor consequential.

The stationary control continues to report the stronger plug-in result: 0.03% oracle excess versus 0.57% for triple feedback at matched records. Theorem 5 characterizes exact conditional allocation feedback at the current policy, not dominance over historical estimation. Section 4 now makes clear that the triple construction reuses an existing batch of at least three independent records. Computing individual policy scores can still carry a model-dependent cost.

  1. Natural code and learned representations. Section 2 and Appendix O.5 separate the general observation model from the experimental grammar. The conditional identities allow heterogeneous prompt/program trace laws and runtime/reward dependence under the stated randomization and policy assumptions. Learned representations require checking regularity and charging score computation. Shared-prompt rollout groups also require the appropriate conditional factorization. The empirical scope remains executed finite programs; natural model-generated code and end-to-end language-model training are distinct settings for extension. Recent contextual rollout scheduling [1] concerns selection and reuse rather than the terminal-censoring decision characterized here.

[1] Lu et al. Contextual Rollout Bandits for Reinforcement Learning with Verifiable Rewards. ICML, 2026.

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Paper summary

This paper studies the problem of reinforcement learning under budget-censored verification. To address the proposed problems, the authors propose a randomized verification allocation framework based on inverse probability weighting to enable unbiased policy gradient updates. In addition, the paper provides a finite-minibatch allocation criterion and establishes the minimum record order required for universally unbiased feedback. The method is also evaluated through experiments.

Critical strengths

The research focus of this paper lies on a practical issues in RL, where training timeouts may lead to incorrect reward assignments. For this problem, authors provide rigorous theoretical analysis to derive a finite-minibatch allocation criterion based on smooth improvement bounds and characterize the minimum statistical record order required for unbiased feedback, and the experiments are designed to support the corresponding theoretical results.

Critical weaknesses
  1. The empirical evaluation is large limited to synthetic environments and a simple task, where the experiment considers a fixed policy with a single verification checkpoint and only a 48-parameter linear softmax policy is employed.

  2. The proposed batch-aware allocation method does not demonstrate a clear advantage over other baselines. Its performance is comparable to Paired CM and Plug-in Φ3\Phi_3, but it is even worse than the performance of Fixed + correction setting.

  3. Although authors derive rigorous theoretical results, the experiments are not sufficient to prove the actual benefits of them. More experiments should be scheduled to demonstrate that the proposed method can achieve faster convergence under the same budget or achieve better final policy performance under comparable training costs. The efficiency of the method can be proven by achieving better performance under restricted conditions.

Questions for authors
  1. Could the authors provide more detailed experimental results to demonstrate the sensitivity analysis about the positivity floor ϵ\epsilon and the allocation step α\alpha. These two hyperparameters are important for the allocation mechanism, but their effects are not sufficiently investigated.

  2. Section 7.2 and M.1 state that the all prompts share the same modular-summation grammar, but this setting is impractical in the real world. Could authors explain how well the proposed method generalizes to different task domains and how robust it would be under heterogeneous task distributions? If not evaluated, could you comment on potential challenges in these new experiment settings?

2 comments

Thank you for recognizing the reference-objective issue and allocation analysis. We address sensitivity and generalization below.

  1. The fixed-policy control and the learning experiment are different. Section 7.1 fixes a two-action policy and uses one checkpoint to isolate the finite-batch criterion. Section 7.2 trains a changing 48-parameter policy with four checkpoints, 720 program sources, and disjoint 36/12/12 training/development/test prompts. The 17,280 reference executions allow exact evaluation. The learning experiment is neither fixed-policy nor single-checkpoint, but remains small and restricted to one constructed grammar. We do not claim cross-domain validation from a within-grammar prompt split.

  2. Positivity-floor and allocation-step sensitivity. The submitted study fixes these parameters and does not supply the requested factorial sweep. We have now added a separate censored-record replay study: ϵ∈0.05,0.10,0.25\epsilon\in{0.05,0.10,0.25}, α∈0.05,0.25,1.25,6.25\alpha\in{0.05,0.25,1.25,6.25}, eight fresh seeds per cell, and logical budget 540. All 96 runs retain the original development-selected policy step 1.35. There is no test-set retuning. Replay exposes only the assigned prefix and any reached endpoint, not hidden outcomes. This is a sensitivity experiment, not live CPU-speed evidence.

At the default α=0.25\alpha=0.25, all three floors give identical trajectories and 78.79% mean held-out success, with a 95% interval half-width of 4.29 points. At α=6.25\alpha=6.25, the respective means are 79.25%, 79.62%, and 80.20%, with half-widths 2.81, 2.35, and 3.13 points. Across the complete grid, means range from 78.20% to 80.20%. These unadjusted intervals are conditional on this corpus, not evidence of a best setting or cross-task robustness. The addendum includes every cell and seed.

The behavior has a direct interpretation. The floor does not change the target gradient while positivity holds, but it constrains allocation and limits inverse weights. The policy second moment is M=∑ahk/shkM=\sum a_{hk}/s_{hk}. The conservative squared allocation-feedback bound has ϵ−3\epsilon^{-3} and ϵ−2\epsilon^{-2} terms (Appendix A.4). Smaller floors therefore permit cheaper schedules but potentially noisier feedback. For a fixed comparator, the bound is D2/(2α)+αNVn/2D^2/(2\alpha)+\alpha NV_n/2, where DD is the allocation-set diameter (Appendix A.6). At the default step the tested floors do not affect the trajectories, whereas the larger step makes the floor consequential. Neither parameter can be chosen optimally from the worst-case bound alone.

  1. What benefit is established? We agree that the batch-aware learner does not beat the corrected fixed schedule in Table 2, and its difference from paired-CMCM remains unresolved. The established benefit is a change in the allocation target and the information needed to estimate its derivative. Theorem 5 gives both an observable construction and a matching unknown-law record-order obstruction. The high-signal control makes that distinction consequential: optimal survival changes from 1 to 0.11178, reducing the finite-batch criterion by 47.6%. At matched records, triple feedback reaches 0.57% excess above its oracle, but the plug-in estimator reaches 0.03%. We retain that stronger baseline. These results establish the mechanism, not faster final policy learning.

  2. Heterogeneous tasks and learned representations. The mathematical model allows an arbitrary fixed prompt distribution and prompt/action-dependent runtime and reward laws. It does not assume the modular-summation grammar or a common completion-time distribution. Conditional randomization, positive endpoint survival, independent whole-prompt records, and policy regularity are the substantive assumptions. Runtime may correlate with correctness.

Those identities do not imply unchanged practical performance under domain shift. Poor pre-execution strata can mix incompatible cost/signal profiles. Rare delayed positives can make estimated moments unstable. Policy changes can make historical plug-in estimates stale. A learned representation changes score norms and their computational cost. The bounded-score and smoothness assumptions must then be justified, rather than transferred from the 48-parameter policy. Same-prompt rollout groups also require care because their shared randomness changes the moment factorization.

HyPeR [1] studies partially observed target rewards, and contextual rollout bandits [2] study adaptive rollout selection and reuse. They support the relevance of these distinct questions, not an empirical generalization claim for our allocator. We ask that the theory be evaluated on its stated observation model, with natural-code performance retained as an open empirical limitation.

[1] Takehi et al. A General Framework for Off-Policy Learning with Partially-Observed Reward. ICLR, 2025.

[2] Lu et al. Contextual Rollout Bandits for Reinforcement Learning with Verifiable Rewards. ICML, 2026.

Thank you for the questions about sensitivity, heterogeneous tasks, and the relation between theory and performance. We have incorporated the response-stage analyses into the paper rather than leaving them in a separate reply. Changes are marked in blue, principally in Sections 2, 4, 7.3, and 8, with the detailed evidence in Appendix O.

  1. The fixed-policy control is separate from policy learning. Section 7.1 fixes a two-action policy and uses one checkpoint to isolate the finite-batch allocation criterion. Section 7.2 trains a changing 48-parameter policy with four checkpoints, 720 program sources, and disjoint 36/12/12 training, development, and test prompts. The 17,280 reference executions permit exact evaluation. We retain this separation, and Section 7.3 now identifies the distinct purpose and accounting of each additional diagnostic. The learning experiment is not fixed-policy or single-checkpoint, although it deliberately uses one controlled program grammar.

  2. The requested positivity-floor and allocation-step sweep. Appendix O.1 and Table 23 report all 96 censored-replay runs: three floors ϵ∈0.05,0.10,0.25\epsilon\in{0.05,0.10,0.25}, four allocation steps α∈0.05,0.25,1.25,6.25\alpha\in{0.05,0.25,1.25,6.25}, and eight fresh seeds per cell. Every run has logical budget 540. The policy step stays at its original development-selected value, 1.35, without test-set retuning. Replay returns only the assigned prefix and any reached endpoint.

At α=0.25\alpha=0.25, all three floors give identical trajectories and 78.79% mean held-out success, with a 95% interval half-width of 4.29 points. At α=6.25\alpha=6.25, the means are 79.25%, 79.62%, and 80.20%, with half-widths 2.81, 2.35, and 3.13 points. Across all twelve settings, means range from 78.20% to 80.20%. The full grid, not a selected setting, is reported. These pointwise intervals measure seed variation conditional on the corpus.

The revised discussion connects this behavior to the mathematics. The floor controls feasible schedules and inverse weights, while the step controls adaptation. The policy second moment contains ahk/shka_{hk}/s_{hk}, and the conservative allocation-feedback bound contains ϵ−3\epsilon^{-3} and ϵ−2\epsilon^{-2} terms. For a static comparator, the allocation regret balances DU2/(2α)D_{\mathcal U}^2/(2\alpha) against αNVn/2\alpha NV_n/2. The inactive floor at the default step and its effect at a larger step are therefore different phenomena. The sweep measures sensitivity, not CPU speed.

  1. What the finite-batch contribution changes. Section 4 now gives the explicit cubic mixture witness behind Theorem 5 and explains why a two-record expectation cannot match it throughout the unknown-law family. An existing policy batch of at least three independent records supplies the attaining estimator without extra verification draws.

The high-signal control makes the change of criterion consequential: optimal survival moves from 1 to 0.11178, reducing the finite-batch objective by 47.6%. At matched records, direct triple feedback reaches 0.57% excess above the oracle and plug-in estimation reaches 0.03%. Both are retained in Table 1. The fixed corrected schedule also retains its leading mean in Table 2. These comparisons distinguish identifying the appropriate allocation functional from identifying the best finite-sample optimizer of that functional.

  1. Heterogeneous tasks and distribution shift. The new paragraph in Section 2 makes explicit that the trace law may vary arbitrarily with the prompt and program, and runtime may correlate with correctness. The common grammar is an experimental choice, not a theorem assumption. Under a fixed prompt mixture, the conditional-randomization identity applies across heterogeneous domains.

Appendix O.5 explains the practical qualifications. Coarse strata can mix incompatible cost/signal profiles. Rare delayed positives can destabilize moment estimates. Changing policies can make historical plug-in estimates stale. Learned representations change score norms and score-computation costs, so bounded-score and smoothness conditions must be assessed for the chosen model. Changing the prompt mixture also requires specifying the target objective and any sampling correction. Multiple completions of one random prompt share randomness and are not interchangeable with the independent whole-prompt records used by the theorem.

The existing strata and overhead controls remain in Appendix M. HyPeR [1] provides related context for learning with partially observed rewards, but the present result specifically characterizes fresh censored feedback for verification allocation. We ask that the revised paper be assessed on this explicit theoretical contribution and the controlled evidence testing its consequences.

[1] Takehi et al. A General Framework for Off-Policy Learning with Partially-Observed Reward. ICLR, 2025.

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Paper summary

The goal is to save verification compute when training a code-writing model with reinforcement learning (RL). Training often counts a check that runs past a short time limit as a failure, so a slow but correct program is labeled wrong. The paper suggests randomly letting some checks run longer (up to the real limit) and reweighting the observed results by how likely they were to be seen, so the reward stays correct on average. It also learns how often to let a check run to the end. More full checks cost more compute, and fewer full checks make the rewards noisier. The paper gives a formula for this balance when training on batches of programs, and shows that learning it from the shortened checks alone needs at least three programs per batch (two without batches). It also shows, in a small example, that rescaling rewards within each group (as in Group Relative Policy Optimization, GRPO) can push the update in the wrong direction when programs are seen with different probabilities. The experiments are small: a two-action toy example and 60 made-up program prompts with a small linear policy, no language model is trained.

Critical strengths
  1. The paper attempts a theoretical anaylsis of verification budgets in RL training because it formalizes when cutting checks short keeps the reward correct on average (Prop. 1), and how often checks should be cut short (Thm. 2 and 5).

  2. The paper points out a real issue because counting a timeout as a failure quietly changes what the model is trained to do: slow but correct programs get punished.

Critical weaknesses
  1. The proposed method does not beat simpler alternatives. In Table 2 (charge 540), batch-aware allocation reaches 78.83% versus 77.61% for full verification, while a fixed schedule with the same reweighting gets 81.01%. Also, in App. M.7 (charge 360), the difference from full verification is not distinguishable from zero (0.22 points).

  2. There is no evidence of real compute savings. The main text only counts abstract "fuel," not wall time or CPU cycles (App. N). When CPU time is matched in the four-prompt study (Table 18), full verification is best: 90.65% vs 86.41% for learned (paired) allocation and 83.49% for the fixed schedule. The only positive CPU result is small (+1.42 points, App. M.7).

  3. The headline gain is artificial. The 13.99-point improvement is measured against a baseline with a very short cutoff (fuel 64 vs a limit of 8192), on a synthetic corpus built so that this cutoff removes every optimal candidate on half the prompts. Naturally, training on false failure labels hurts the baseline. Simply verifying everything, with no early cutoff, recovers almost the same benefit (77.61% vs 64.83%).

  4. The theoretical novelty is minimal. The tools are standard, and the paper says this: inverse probability weighting, a minibatch extension of Beatson & Adams (2019). The GRPO's normalization biases updates is also already known.

as a reviewer, due to limited time, i was not able to check all theoretical results even though they look correct. Most of technical part, just simply coming from arithmatics in my opinion from known technique, no fancy or newly developed technique. I also didn't much like their description, for example, in equation (8), 'Flattening the coordinates gives the useful expression' <- this is basically coming from a * (b + c) = ab + ac, basic arithematics, why should we say something like useful expression. this is just my taste, i would write, simply multiplying two equations in 7, -> we get 8 something like that.

Questions for authors
  1. Can you show one setting where learned allocation beats both full verification and the fixed corrected schedule, measured in CPU time?

  2. Can you run one experiment with a small language model on real code, where timeouts happen naturally, and report how often they happen?

  3. How does the 13.99-point gain change if the negative-label baseline uses a realistic timeout instead of fuel 64 against a limit of 8192?

  4. Beyond applying paper [1] to a minibatch, what is the new technical step in Theorems 2 and 5? I actually do not see any novelty here.

  5. Is there any evidence that a lower allocation criterion leads to better final success?

[1] Alex Beatson and Ryan P. Adams. Efficient optimization of loops and limits with randomized telescoping sums. In Proceedings of the 36th International Conference on Machine Learning, volume 97 of Proceedings of Machine Learning Research, pp. 534–543, 2019.

5 comments

Thank you for distinguishing soundness from significance. We agree that the paper does not establish general training acceleration. Its main result is a characterization of the feedback needed to learn a computation-aware allocation without changing the reference reward objective.

  1. What is new beyond Beatson and Adams? We explicitly credit their randomized telescoping estimator, improvement-per-computation analysis, and online tuning [1]. Theorem 2 is a finite-minibatch specialization of that analysis. Equation (8) is an elementary expansion that exposes convexity, not the claimed theoretical advance.

The additional question in Theorem 5 is whether the allocation gradient itself can be estimated conditionally without bias from censored records when the trace law is unknown. For independent policy records, Φn=CM+(n−1)∣γ∣2,γ=∇J.\Phi_n=C{M+(n-1)|\gamma|^2},\qquad \gamma=\nabla J. The extra allocation derivative is (n−1)∇C∣γ∣2(n-1)\nabla C|\gamma|^2. A distinct triple vi⟨gj,gk⟩v_i\langle g_j,g_k\rangle estimates it without unknown completion-time or reward coefficients.

The matching necessity argument is explicit, not inferred from the construction. Appendix A.5 gives admissible trace-law mixtures preserving the fixed policy marginal with C=A+dqλC=A+dq\lambda, M=λ/(8q)M=\lambda/(8q), and γ=λ/4\gamma=\lambda/4, with fixed cost constants A,d>0A,d>0. Thus ∂log⁡qΦn=−Aλ/(8q)+(n−1)dqλ3/16.\partial_{\log q}\Phi_n=-A\lambda/(8q)+(n-1)dq\lambda^3/16. Under a fixed observation kernel, any parameter-independent estimator using at most two independent records has expectation at most quadratic in λ\lambda. It cannot equal this cubic functional for every mixture. Three records attain it. Classical polynomial-functional reasoning is credited to Halmos and Hoeffding. The contribution is this allocation-specific characterization, not a new general statistical principle. It concerns exact conditional unbiasedness, not a prohibition on plug-in learning or a requirement of three additional verifications per update.

The distinction has a concrete consequence: Proposition 3 changes optimal survival from 1 to 0.11178 and reduces Φ3\Phi_3 by 47.6%. This is an allocation-bound separation, not a measured training speedup. The known-cost control is expressly not the lower-bound witness.

  1. Simpler baselines and CPU savings (questions 1 and 5). Your reading of Table 2 is correct: fixed correction has the highest mean, 81.01%, versus 78.83% for batch-aware allocation and 77.61% for full verification. In the separate two-second CPU study, the corresponding means are 78.83%, 83.05%, and 81.63%. Reaggregating its eight matched seeds gives batch-aware minus full = 1.42 points [0.09, 2.74], but minus fixed = 4.22 [-1.80, 10.25]. These unadjusted intervals do not establish superiority to both. We retain the four-prompt CPU loss as well.

A smaller allocation criterion does not order final accuracies along different training trajectories. Theorem 2 orders optimized local smooth lower bounds. Section 5 goes further: for a different policy update, an 80.9% decrease in CMCM can accompany a 16.2% increase in the relevant curvature penalty. These distinctions are results of the paper, not an inference of efficiency from unbiasedness.

  1. The short-timeout control (question 3). The 13.99-point gap isolates objective misspecification, not an advantage over correctly labeled full verification. Full verification's recovery of most of that gap is consistent with this purpose. An additional calculation on the existing held-out trace bank varies the cutoff: labeling interrupted runs as failures excludes every reference-optimal candidate on 6/12 prompts at fuel 64, 4/12 at 512, 1/12 at 2048, and 0/12 at 4096. This is a structural cutoff analysis, not a new learning curve or evidence that these cutoffs are realistic. The final-success gap at those alternative cutoffs remains unmeasured.

  2. Natural code and normalization (question 2). No natural-code timeout prevalence or language-model fine-tuning result is reported. The constructed grammar tests a mechanism, not its frequency in deployment. Recent RLVR rollout-scheduling work [2] addresses a related computational decision, but cannot validate our terminal-censoring mechanism. Likewise, GRPO bias is already studied [3]. Our narrower normalization result is a fixed-prompt direction reversal caused by unequal censoring propensities despite unbiased corrected rewards.

We ask that significance be assessed on the feedback characterization and its explicit consequences, without attributing a general CPU-speed claim to the paper.

[1] Beatson and Adams. Efficient Optimization of Loops and Limits with Randomized Telescoping Sums. ICML, 2019.

[2] Lu et al. Contextual Rollout Bandits for Reinforcement Learning with Verifiable Rewards. ICML, 2026.

[3] Liu et al. Understanding R1-Zero-Like Training: A Critical Perspective. COLM, 2025.

Thank you for the detailed response.

I appreciate the clarification regarding Theorem 5. I initially thought the theoretical results were mostly straightforward extensions of existing techniques. I now see that Theorem 5 provides an additional result on the minimum number of independent records needed for unbiased gradient estimation. Although the underlying techniques are classical, I agree that this is a meaningful theoretical contribution.

Regarding the experiments, I still have some concerns. As the authors also acknowledged, the learned allocation does not consistently outperform simpler baselines, particularly the fixed corrected schedule. The additional CPU-matched result is encouraging, but I don't think the current evidence is strong enough to demonstrate a clear computational advantage.

I also understand that the 13.99-point improvement is meant to demonstrate the effect of incorrect timeout labels rather than computational efficiency. That kinda makes sense. But, I still think the practical significance is unclear. The experiments are mostly synthetic, and there is no evaluation with actual language-model training or realistic code-generation tasks. Without such experiments, it is difficult to tell how useful the proposed approach would be in practice.

Overall, the rebuttal addressed some of my concerns, particularly regarding the novelty of Theorem 5. I have slightly increased my score from 1 to 2. However, my main concern about the practical significance remains, so I still lean toward rejection.

Thank you for reconsidering Theorem 5 and recognizing its theoretical contribution. We have made a focused revision, marked in blue, that addresses your remaining concerns about practical significance. The main additions are Section 7.3 and Appendix O. Out original theorem statements, proofs, and experimental comparisons are retained, no change.

1. What the theorem enables in practice. Section 4 now states the distinction directly: this is a result about the allocation gradient, not another unbiased reward estimator. It includes the explicit cubic trace-law witness and explains that, when the policy batch already contains at least three independent records, the construction reuses those records without additional verification draws. Theorem 2 credits the smooth-improvement argument of Beatson and Adams [1]. We also simplified the wording preceding Equation (8).

The practical consequence is a choice of allocation criterion. In the positive-reward control, the conventional product selects full verification, while the ordinary minibatch criterion selects survival 0.11178 and reduces that criterion by 47.6%. Censored feedback learns the changed allocation. Theorem 2 orders optimized local smooth bounds at a fixed policy. Final success is assessed separately in Tables 2 and 25. Table 1 retains the stronger stationary plug-in result alongside direct feedback. Thus the contribution supplies both an information requirement and a constructive way to meet it, rather than asserting that one estimator should replace every simpler alternative.

2. CPU evidence and the fixed corrected baseline. Section 7.3 now brings the measured-CPU comparison into the main paper. Appendix O.3, Figure 11, and Table 25 report all seven methods, complete saved-policy learning curves, and paired endpoint uncertainty. At the nominal two-second target, batch-aware allocation reaches 83.05%, versus 81.63% for full verification and 78.83% for fixed correction. The paired differences are +1.42 points [0.09, 2.74] and +4.22 [-1.80, 10.25], respectively. Paired-CM reaches 83.00%, and reward-only allocation has the largest mean, 84.67%.

The fixed corrected schedule remains the strongest mean in the separate slow-optimal, logical-work study. These are different experiments, and the revision labels their budgets and populations explicitly. We agree that the CPU comparison does not settle superiority to the fixed schedule. Its role is to expose the complete computational comparison, including allocation and solver overhead, rather than infer runtime savings from logical fuel or an allocation objective.

3. Dependence on the short training cutoff. Appendix O.2 and Table 24 now vary the cutoff across eight values on the existing held-out bank. Negative timeout labels exclude every reference-optimal candidate on 6/12 prompts at 64, 4/12 at 512, 1/12 at 2048, and 0/12 at 4096. This gives the precise dependence on cutoff, rather than relying only on the most restrictive setting. The 13.99-point training difference remains attached to the cutoff-64 experiment. The additional analysis compares reward objectives exactly, not newly trained policies at each cutoff or natural-code timeout frequencies.

4. When is allocation worth using? Section 8 and Appendix O.4 now connect the existing regime theorem to a concrete decision. In its one-checkpoint model, full verification is optimal when (n−1)∥γ∥2/a≤c0/d,(n-1)\|\gamma\|^2/a\le c_0/d, where aa is the uncensored gradient second moment and dd is verification cost. Above this boundary, the criterion favors thinning until the positivity floor binds. We describe an optional, separately charged pilot for comparing schedules and diagnosing concentrated inverse weights. This explains when a simpler corrected schedule or full verification is the appropriate choice.

5. Realistic code and learned policies. The revision's empirical scope is executed finite programs, supplemented by censored replay and recorded CPU trajectories, rather than language-model fine-tuning. Section 2 and Appendix O.5 clarify the transferable assumptions: prompt/program-dependent trace laws, logged conditional randomization, positivity, and independent whole-prompt records. Runtime may depend on correctness. Learned representations additionally require model-specific score regularity and complete score-computation accounting. Contemporary rollout scheduling [2] addresses a related but distinct selection/reuse problem.

We hope these changes make the contribution's significance clearer: a sharp feedback requirement, an attaining construction, and concrete allocation and labeling decisions whose consequences are measured separately.

[1] Beatson and Adams. Efficient Optimization of Loops and Limits with Randomized Telescoping Sums. ICML, 2019.

[2] Lu et al. Contextual Rollout Bandits for Reinforcement Learning with Verifiable Rewards. ICML, 2026.

Comments on the paper

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Follow-up response

We thank the Area Chair and all three reviewers for the careful reading and discussion. We have incorporated the requested clarifications and analyses into the revised manuscript, with changes marked in blue. The main points are summarized below.

Reviewer CBUC, and contribution and practical benefit. We appreciate the recognition of Theorem 5’s theoretical contribution. The revised paper distinguishes the experiment that isolates the finite-batch correction from the comparison of complete training procedures.

Section 7.1 and Table 1 hold the policy fixed and ask whether censored feedback can learn the changed allocation. The table reports excess above the oracle finite-batch objective, in percent, where lower is better. Entries are means with 95% interval half-widths over 40 seeds.

Allocation feedback12,000 recordsCharged work 1,200
Paired-CM90.86 ± 0.0090.86 ± 0.00
Triple, finite-batch criterion0.57 ± 0.241.12 ± 0.38
Plug-in, finite-batch criterion0.03 ± 0.020.05 ± 0.03
Known-cost pair0.03 ± 0.010.15 ± 0.08

Reading the results at the stated budgets:

  • The allocation decision changes substantially. The conventional criterion selects full verification, whereas the finite-batch optimum has survival 0.11178 and an allocation objective 47.6% lower. At matched charged work, triple feedback achieves 1.12% mean excess above this optimum.
  • Simpler estimators can also exploit the criterion. The plug-in and known-cost methods perform strongly. Theorem 5 establishes the sharp two-versus-three-record requirement for universally conditionally unbiased allocation feedback under the unknown-law model, with three required for the finite-batch criterion when n>1n>1. Known cost information and historical estimation provide useful alternatives.
  • The CPU study measures a different outcome. At the nominal two-second process-CPU target, averaging over eight seeds, reward-only, batch-aware, and Paired-CM achieve 84.67%, 83.05%, and 83.00% mean success. Full verification achieves 81.63%, with a paired batch-aware improvement of 1.42 points and a 95% interval of [0.09, 2.74]. Appendix O.3, Figure 11, and Table 25 report all seven methods, complete saved-policy curves, and paired endpoint intervals.

At the CPU corpus’s initial policy, the CM-optimal schedule is already within approximately 0.003% of the finite-batch optimum (Appendix M.6). This diagnostic helps interpret the close comparison in that setting. The frozen-policy calculation and the complete training trajectories answer complementary questions.

For the cutoff question, Appendix O.2 and Table 24 add eight exact comparisons on the held-out trace bank. Labeling timeouts as failures excludes every reference-optimal candidate on 6/12 prompts at cutoff 64, 4/12 at 512, 1/12 at 2048, and 0/12 at 4096. This makes the dependence on the training limit explicit.

Reviewer nKYJ, and sensitivity and heterogeneous tasks. Appendix O.1 and Table 23 report the full 96-run censored-replay sweep: three positivity floors, four allocation steps, and eight seeds per setting. The policy step remains fixed at its development-selected value. Mean success ranges from 78.20% to 80.20% across the twelve settings.

The fixed-policy control above is separate from Section 7.2, which trains a changing 48-parameter policy with four checkpoints. Section 2 and Appendix O.5 clarify the prompt- and program-dependent trace laws and the randomization, positivity, independence, and score-regularity assumptions needed for heterogeneous tasks and learned policies.

Reviewer VuUB, and computation, variance, and practical use. The CPU curves use the recorded runs and include verification, policy updates, score computation, and allocation overhead. Section 4 now explains that the three-record construction reuses an existing policy minibatch of at least three independent records, without additional verifier runs. Its evaluation is linear in minibatch size after score computation.

Section 8 and Appendix O.4 connect allocation to signal strength and fixed overhead, and describe an optional, separately charged pilot for comparing schedules and identifying concentrated inverse weights. The revision also preserves the strong historical plug-in comparison, so readers can assess the choice between direct unbiased feedback and accumulated moment estimates.

Section 7.3 summarizes the additional findings in the main text. Together, the revisions clarify when finite batching changes the appropriate allocation, what observations are needed to learn it, and how these choices behave under censored verification. We appreciate the discussion and welcome any final questions.

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

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