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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 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.
- 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.
- When does rare-verification variance outweigh the saving? Section 8 now highlights the boundary from Proposition 3. With one checkpoint, common survival , deterministic verification cost , overhead , and , define and . Full verification minimizes the finite-batch criterion when . Above that boundary, the optimum is 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 , and the generic allocation-feedback bound can grow as .
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.
- 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.
- 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.
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.
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-CM, 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.
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) 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.
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.
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.