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Under review as a conference paper at ICLR 2027

Optimizing What Policies Learn From: Recoverability-aware Rollout Intervention Learning

Abstract

Critic-free group-based RL has become a scalable paradigm for LLM post-training. However, its effectiveness is constrained by a major limitation: rollouts are allocated uniformly even though their learning value varies substantially across tasks and trajectory states. Despite recent efforts to allocate rollouts adaptively across tasks, existing methods suffer from two core gaps: the non-stationary gap, which calls for intervention strategies from learning an evolving policy rather than relying on heuristic rules, and the non-scalar gap, which calls for structured control over where and how to intervene rather than merely deciding how many rollouts to generate. To close these gaps, we introduce Recoverability-Aware Intervention Learning (RAIL), a training-time framework that turns rollout generation into a learnable intervention process by optimizing structured decisions according to their realized recoverability gains. Specifically, RAIL first casts intervention selection as an online contextual-bandit problem and then trains a recoverability controller from intervention traces collected through a shadow-to-live procedure, performing intervention learning while policy evolves. Finally, we evaluate RAIL for its effectiveness, adaptivity, expressiveness, and efficiency, showing consistent gains with constrained rollout budgets. Together, our results establish recoverability-aware intervention as a principled path toward more informative rollout generation, enabling post-training to optimize from stronger and less redundant learning signals.

Primary area:
reinforcement learning
Keywords:
Dynamic Rollout Allocation, Agentic Reinforcement Learning, Recoverability-Aware Intervention Learning

Reviews

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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.
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2
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3
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Paper summary

This paper proposes Recoverability-Aware Intervention Learning (RAIL) to improve rollout efficiency in LLM reinforcement learning. RAIL introduces an online recoverability controller that learns from intervention outcomes to adaptively select branching locations, rollout budgets, and decoding strategies. A shadow-to-live procedure enables the controller to adapt alongside policy optimization. Experiments across four agentic benchmarks demonstrate improved task success rates with fewer rollouts compared to existing baselines.

Critical strengths

S1. The problem formulation, methodological presentation, and overall organization of the paper are clear. The authors have evidently put substantial effort into this work.

S2. The paper addresses an important problem and proposes a relatively simple and clearly presented method.

Critical weaknesses

W1. Limited theoretical contribution

The theoretical analysis in Appendix C largely relies on strong assumptions. In particular, Assumption C.7 directly assumes the cumulative tracking-error bound: ϵT≤O~(T∣B∣+DT+AT).\epsilon_T \leq \widetilde{O}(\sqrt{T|\mathcal{B}|}+D_T+A_T).

Theorem C.8 then follows from: RegT≤2ϵT+∑ρt.\mathrm{Reg}_T \leq 2\epsilon_T + \sum\rho_t. However, the paper does not prove that the proposed controller satisfies the assumed bound. Similarly, Proposition C.9 follows directly from assuming persistent per-step regret. Moreover, lower recoverability regret is not theoretically linked to improved GRPO convergence or final policy performance. Thus, the theoretical analysis provides limited substantive guarantees for the proposed method.

W2. Insufficient justification of the recoverability objective

Section 2.1 defines recoverability through reward-variance improvement:

Δθ(z,b)=E[I(Yb)−I(Y∅)∣z,b,πθ].\Delta_\theta(z,b)=\mathbb{E}[I(Y_b)-I(Y_\varnothing)\mid z,b,\pi_\theta].

However, Appendix B.3.3 implements a different, cost-penalized objective:

\quad d(Y)=|\bar{R}_Y-0.5|.$$ Although related under binary rewards, these objectives are not equivalent and may favor different interventions. Furthermore, higher reward variance does not necessarily imply better policy improvement. The sampling-distribution mismatch introduced by temperature and top-p interventions, as acknowledged in Appendix D.1, also lacks empirical evaluation. **W3. Insufficient comparison with closely related methods** The paper compares against several adaptive rollout baselines but excludes closely related learned allocation methods such as TRACE, 3SPO, and IGRPO, despite discussing them in Appendix A. Comparisons with these methods are important for establishing the novelty and effectiveness of the proposed controller. **W4. Insufficient evidence for structured intervention** Table 2 shows that the four-option scalar variant outperforms full RAIL on AgentBench-OS (34.11% vs. 33.30%), questioning the consistent benefit of structured intervention. Moreover, improvements over strong baselines are sometimes modest, and experiments are limited to Qwen3-4B-Instruct. Stronger ablations and evaluations across model scales would better support the claims. **W5. Limited efficiency evaluation and reproducibility** The efficiency analysis primarily reports rollout counts without wall-clock time, GPU-hours, or throughput, making actual computational savings unclear. Additionally, no public code is provided, and several training configurations remain insufficiently specified, limiting reproducibility. **Minor** 1. **Figure clarity.** Figure 2 is overly complicated, with excessive decorative elements that make the overall workflow difficult to follow. The authors should simplify the visualization. 2. **Related Work.** The Related Work section is entirely placed in the appendix, leaving insufficient discussion of the most closely related methods in the main text. The authors should better highlight these comparisons in the main paper.
Questions for authors
  1. How can Assumption C.7 be justified for the proposed controller, and how does the regret bound relate to actual policy improvement?
  2. Why does the implementation use a different recoverability objective from the theoretical formulation? How does the sampling-distribution mismatch affect training?
  3. Can the authors provide comparisons with TRACE, 3SPO, and IGRPO?
  4. Why does the scalar variant outperform full RAIL on AgentBench-OS in Table 2?
  5. Can the authors report wall-clock time and GPU-hours, and release the code and complete training configurations?
6 comments
AuthorsOpenReview ↗

Rebuttal Part - [1/6] Theoretical analysis

We thank the reviewer for the careful reading. We agree that our current presentation does not clearly separate the tracking assumption from the result that follows from it. To state the scope of the analysis precisely:

  • We assume that the online controller has cumulative tracking error ϵ_T = Σ_{t=1}^{T} E[ max_b |f̂_t(z_t, b) − f_t(z_t, b)| ] (Assumption C.7).
  • We prove that the intervention regret satisfies Reg_T ≤ 2ϵ_T + Σ_{t=1}^{T} ρ_t, where ρ_t is the exploration mass at step t (Theorem C.8).
  • We do not prove that the implemented MLP controller attains a given tracking rate under partial feedback and policy drift. Assumption C.7 and Theorem C.8. Assumption C.7 is not implied by finite actions and sufficient exploration; it is the condition under which the controller's prediction error can be converted into intervention regret. Theorem C.8 uses the standard decomposition noted by the reviewer: if the controller's prediction error over all interventions at step t is at most e_t, the gap between its chosen intervention and the truly optimal one is at most 2e_t, and summing over steps gives the bound above. The role of this result is to connect the controller's prediction quality to the quality of its structured intervention decisions: it identifies cumulative controller tracking error as the key quantity controlling structured-intervention regret. It does not prove that the neural controller satisfies the tracking bound, and sublinear regret follows only when ϵ_T and the cumulative exploration term are sublinear. We will revise Theorem 3.1 to state this condition explicitly and present the rate in Assumption C.7 as a conditional corollary.

We do not prove a full tracking rate for the neural controller under partial feedback. The effect of stale traces can nevertheless be separated from this learning assumption. With an effective memory of W, each change in the recoverability function affects at most W later estimation windows, giving an O(W · D_T) contribution from stale supervision. The remaining approximation and partial-feedback estimation errors are captured by the tracking condition. We will state this separation more clearly in Appendix C.2 and D.2. Figure 3 provides finite-run evidence that online updating improves prediction accuracy over a frozen controller, but it is not a proof of Assumption C.7.

Proposition C.9. The reviewer is right that this result follows by summing a persistent per-step gap. It is not intended as a standalone lower-bound result. Its purpose is to state the condition under which a fixed rule accumulates linear recoverability regret: if its mismatch persists on a constant fraction of training steps, the rule cannot reduce this mismatch through outcome feedback. Appendix C.2 discusses how this can arise for proxy-driven and restricted intervention rules. Figures 3 and 7 provide finite-run evidence for these mismatch mechanisms rather than proving the asymptotic condition. We will restate Proposition C.9 as a conditional observation and clarify its role.

Link to GRPO. We agree that the regret analysis does not provide a convergence guarantee for GRPO or a guarantee on final policy performance. The connection is through the immediate learning signal. For the centered and leave-one-out advantages analyzed in Appendix C.1, the expected squared reward-dependent advantage is proportional to reward variance. In particular, an all-equal reward group has zero centered advantages and provides no reward-dependent relative signal. Lower recoverability regret therefore means a smaller shortfall, relative to the best available intervention, in the reward variance exposed to the policy update. The final-performance improvements in Table 1 are empirical results rather than consequences of the regret theorem.

AuthorsOpenReview ↗

Rebuttal Part - [2/6] Insufficient justification of the recoverability objective

Definition and implementation. We hope to clarify that Equation (2) is the general definition of recoverability, while Appendix B.3.3 is its specific implementation for the binary rewards used in all our experiments. For a rollout group Y with success rate p(Y), the reward variance is I(Y) = 1/4 − d(Y)² with d(Y) = |p(Y) − 1/2|. Hence, for the groups Y and Y′ before and after an intervention,

I(Y′) − I(Y) = (d(Y) − d(Y′)) × (d(Y) + d(Y′)).

The first factor is the distance reduction used in the implementation, and the second factor is never negative. The two therefore always have the same sign, and at the same state they rank intervention outcomes in the same order, so the distance reduction is an order-preserving binary surrogate of the reward-variance gain. Without the cost term, they never favor different interventions at the same state.

The cost term. The cost term is not part of the definition of recoverability and appears only in the implemented label, y = d(Y) − d(Y′) − λ · C(b), where C(b) is the number of added continuations and λ = 0.005 in the training. It is the only part that can change which intervention is preferred, and this is intended. Without it, the label would not account for the number of continuations an intervention consumes, so a larger branch budget, which has more chances to expose a differing outcome, would tend to be preferred even when a smaller budget achieves a similar gain. With it, a larger budget is chosen only when its extra gain pays for its rollouts. With it, a larger budget is chosen only when its extra gain pays for its rollouts. We will describe the implemented label as a cost-regularized intervention utility and distinguish it from the recoverability definition in Section 3.1.

Reward variance and policy improvement. It is true that higher reward variance does not by itself guarantee better policy improvement, and we do not claim it does. It is an immediate, local proxy for the learning signal that an intervention exposes: when all rewards in a group are equal, their centered advantages vanish and the group provides no reward-dependent relative-advantage signal (Appendix C.1), and Appendix C.1 relates reward variance to the size of the relative advantages and of the projected gradient. Appendix D.5 discusses where this reading holds and where it weakens, and Table 1 reports the final performance obtained with this choice.

Sampling mismatch. We agree that varying temperature and top-p introduces additional sampling mismatch beyond the default decoding regime. As Appendix D.1 states, the resulting update is only approximately on-policy with respect to the token-level sampling distribution. We do not apply importance correction because top-p truncation may violate support requirements and sequence-level correction can have high variance. We will make clear that this is a practical design choice rather than an unbiased on-policy update. The same mismatch already arises in standard GRPO training whenever rollouts are sampled with temperature or top-p settings that differ from the training policy, as in the default regime of our experiments (Appendix B.3.1). We have not evaluated corrected and uncorrected updates separately. The component-removal variant without decoding interventions in Table 2 removes the additional mismatch together with the decoding interventions themselves, so it shows that their net effect is positive on both AgentBench benchmarks but does not isolate the mismatch. We will state this limitation in Appendix D.1.

AuthorsOpenReview ↗

Rebuttal Part - [3/6] Insufficient comparison with closely related methods

We agree that comparisons with TRACE, 3SPO, and IGRPO are important, since they also learn where to allocate rollouts within a trajectory. These works appeared on arXiv shortly before our submission, so we discussed them as concurrent work in Appendix A. Following the reviewer's suggestion, we have now trained all three methods with Qwen3-4B-Instruct and evaluated them on AgentBench-DB and ToolQA-Coffee with the same test sets and evaluation protocol as Table 1. We reimplemented the three methods in our training framework following their papers, keeping each method's rollout allocation and policy-update rule, and selected the learning rate and checkpoint per method; the adaptations to our one-task-per-step setting will be listed in Appendix B.2. The GRPO rows are taken from Table 1.

MethodAgentBench DBToolQA Coffee
Overall SRSELECTINSERTUPDATEOverall SRHard
Qwen3-4B53.42±0.2842.25±0.5040.82±0.0078.79±0.8274.75±0.6655.00±1.22
TRACE57.92±0.2840.25±0.4347.50±0.5086.00±0.0083.00±0.3571.00±0.71
3SPO58.17±0.3744.25±0.4346.75±0.8383.50±0.5082.75±0.7570.75±1.64
IGRPO57.83±0.3743.75±0.8346.00±0.7183.75±0.4383.50±0.3572.00±0.71
RAIL61.67±0.4150.50±1.2951.00±0.8283.50±0.5886.75±0.5678.50±1.12

Each learned method improves over GRPO at its maximum rollout budget (GRPO-16 for TRACE, GRPO-8 for 3SPO and IGRPO), which confirms that learned state-level allocation helps in agentic RL. RAIL still achieves the best overall SR on both benchmarks and on most splits. We attribute this to what the controller learns. TRACE and 3SPO score a state by how likely it is to succeed, and IGRPO expands a branch by its information gain. RAIL instead learns the realized gain of an intervention, that is, whether branching at a state with a given budget and decoding setting actually yields more reward variance for the policy update. In our implementation, TRACE and IGRPO optimize the policy with group-relative advantages over all leaves of the rollout tree, 3SPO uses its step-wise post-step update, and RAIL keeps the standard GRPO objective.

We will add these results to Table 1 and the implementation details of the three baselines to Appendix B.2. We hope this addresses the reviewer's concern.

Reviewer_49MMOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The authors propose Recoverability-Aware Intervention Learning (RAIL), which is a general rollout intervention framework for critic-free, group-based RL. They identify two limitations of existing heuristic methods, the non-stationary gap, where intervention rules fail to adapt as the policy evolves during training, and the non-scalar gap, where intervention decisions focus primarily on rollout count. In contrast, RAIL first formalizes recoverability as the expected improvement in reward contrast produced by an intervention relative to default rollouts, and then learns a parametric model to predict this gain for candidate interventions. To fit the predictor, RAIL further introduces a warmup phase, the Shadow Mode, where they apply a heuristic policy to progressively explore interventions and collect the initial training data. Empirical results show consistent performance gains under constrained rollout budgets while maintaining decent computational efficiency.

Critical strengths

The paper provides a principled formulation of rollout intervention. The paper organizes rollout intervention around recoverability and provides a detailed justification for using reward contrast to measure intervention gains. This offers a unified perspective on the motivation behind existing methods, such as DAPO's dynamic sampling, while extending it to learned, adaptive intervention selection.

The proposed formulation permits potential extensibility. The framework provides clear opportunities for extension, through its intervention space. Although the experiments focus on rollout count and decoding regime, the formulation could also potentially accommodate additional choices, as shown in appendix, such as prompting style, verifier-guided repair, or rollback actions. The framework offers a common mechanism for selecting among different intervention strategies.

Critical weaknesses

While the paper presents a principled framework and strong empirical results against the baselines, a few minor concerns remain: The framework is built around recoverability, which is a measure of the richness of learning signal. However, its formulation is closely related to the learnability measure introduced in LILO (https://arxiv.org/pdf/2502.12272). Essentially, recoverability seems like the improvement in learnability compared to an unperturbed baseline. This raises the question of why the authors use this learnability improvement over baseline rather than learnability itself to guide intervention selection, and what benefits this choice provides. The authors should also cite LILO and clarify the differences between the two measures.

Another minor concern is that the ablations do not fully isolate the contribution of learned intervention selection. Although the paper includes a broad set of baselines and ablations on adaptivity and expressiveness, it is unclear whether the comparisons use exactly the same intervention space. The baselines are described as controlling either rollout budget or decoding temperature, whereas RAIL jointly selects both. Consequently, some gains could arise from access to a richer intervention space. Comparisons against selectors operating within the same space, even with some simple methods, such as the paper's own shadow-mode heuristic, would further strengthen the results.

Questions for authors
  1. What motivates using recoverability, the improvement in learnability compared to an unperturbed baseline, instead of the learnability itself? What benefits does this choice provide?
  2. Could the authors compare RAIL against some selectors operating over the same intervention space under comparable rollout budgets?
2 comments
AuthorsOpenReview ↗

Rebuttal Part - [1/2] Recoverability and learnability (LILO)

Thank you for pointing us to LILO. We will cite LILO and clarify the relationship between the two measures in Section 2.1 and Appendix C.1. Recoverability follows the same line of work that measures the learning signal of a task by its reward variance. As discussed in Appendix C.1, we adapt this idea from the variance analysis of VIP, which shows that the binary reward variance p(1−p) governs the projected-gradient variance of group-based RL. LILO uses the absolute reward variance of a question as its learnability, whereas RAIL uses the intervention-induced change in this quantity relative to default continuation.

The difference lies in the decision being made. LILO uses absolute learnability to identify informative questions for training. RAIL instead needs to determine whether a particular intervention at a given trajectory state adds a learning signal beyond default rollout generation. If absolute learnability were used directly as the intervention utility, it could favor states that are already informative even when additional branching adds little signal. Conversely, it could reject an all-success or all-failure state even when a particular intervention can make it informative. Recoverability measures exactly this difference.

The main benefit of this choice is that the default rollout process becomes a natural zero baseline, so the utility gate decides whether an intervention is worth more than no intervention, and RAIL skips branching where little can be gained (Section 3.2). This mechanism contributes to RAIL's ability to avoid unnecessary branching, consistent with the rollout-efficiency results in Table 3.

AuthorsOpenReview ↗

Rebuttal Part - [2/2] Where the gains come from

Thank you for this observation. The reviewer is right that the baselines in Table 1 control a single intervention dimension while RAIL jointly selects both, so Table 1 alone does not isolate the contribution of learned selection. As discussed in Section 2.2, the limitation of prior work is not only that some intervention dimensions are omitted, but that there is no principled mechanism to coordinate them effectively. Existing methods either focus on a single dimension, such as rollout count or decoding temperature, or these choices co-exist but as separate decisions (like in the shadow mode). RAIL addresses this through the design of its controller. Each intervention is represented as a structured action code over its dimensions, and every candidate is scored by the same quantity, its predicted recoverability gain at the current state (Section 3, Appendix B.3). Choices along different dimensions are therefore compared on a common scale and selected jointly, rather than set by separate heuristics.

Table 2 provides two complementary controls that help separate these effects. In Table 2 (Section 4.2), we first ran single-dimension variants, in which the controller selects only the branch budget or only the decoding regime. Both perform worse than the full RAIL on OS and DB. This control isolates the contribution of the richer intervention space under the same learned controller; it does not compare learned selection with heuristic selection. Second, the longer-shadow variants use the same structured intervention space but rely on the heuristic for more training and on the learned controller for less. Their lower performance suggests that the learned controller adds value beyond simply having access to the richer intervention space. Figure 3 (Section 4.2) examines the selector from a third angle: a controller trained only in the shadow phase and then frozen gradually loses prediction quality as the policy evolves, whereas the online-updated controller keeps tracking the realized gains, which isolates the role of online updating relative to a frozen controller. These controls do not include a heuristic-only selector over the full space for the entire training, and we will state this scope and what each control isolates explicitly in Section 4.2.

Reviewer_4QHEOpenReview ↗
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1
Confidence
2
Informativeness
2
Presentation
1
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2
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Paper summary

This paper proposes RAIL, a framework for adaptive rollout generation for LLM post-training. RAIL formulates rollout sampling as an online contextual-bandit problem, where a lightweight controller predicts the increase in empirical reward variance from different sampling strategies then greedily selects the one that maximizes this term. Experiments across four agentic benchmarks show improvements in task success rates and average rollout counts over several existing baselines.

Critical strengths
  • Improving the efficiency of rollout generation is an important direction for LLM reinforcement learning.
  • The reported improvements across four benchmarks are encouraging.
Critical weaknesses
  • The paper characterizes existing approaches as predominantly heuristic or restricted to scalar rollout allocation, but does not adequately discuss or compare against several closely related methods that perform adaptive data-selection [A, B, C]. A more comprehensive discussion and comparison would help establish the precise novelty and contribution of the proposed method.
  • While the formal definition of recoverability in Equation (2) uses the change in empirical reward variance, the implementation in Appendix B.3.3 uses the reduction in distance of the empirical success rate to 0.5, with an additional cost penalty. This is misleading to readers, especially since this detail is hidden in the appendix and not mentioned in the main paper. The paper should clarify this discrepancy and better justify its choice of utility signal.
  • The paper is written in a highly compressed, sometimes telegraphic style, and introduces new terminology for established concepts in the literature that make it difficult for a reader to understand and compare to existing works. For example, "reward contrast" refers to empirical reward variance, and the "shadow-to-live" procedure is essentially a heuristic warm-up followed by online controller deployment. This terminology makes it unnecessarily difficult to identify the paper’s contributions.
  • The theoretical contributions are questionable.
    • Theorem 3.1 is underspecified. It states “Under finite-action contextual-bandit feedback with sufficient intervention exploration, the regret of the controller satisfies”, but having finite-action bandit feedback and sufficient exploration is not enough to guarantee sublinear regret.
    • The regret analysis in Appendix C.2 relies on Assumption C.7, which postulates a cumulative tracking-error bound of essentially the same order as the claimed regret guarantee. The subsequent theorem then applies a standard decomposition relating greedy action-selection regret to prediction error. The main technical difficulty of establishing the assumed tracking bound for the proposed online controller under partial feedback and policy non-stationarity is not addressed.

[A] Lu, Xiaodong, et al. "Contextual Rollout Bandits for Reinforcement Learning with Verifiable Rewards.” ICML, 2026

[B] Sun, Yifan, et al. "Improving data efficiency for llm reinforcement fine-tuning through difficulty-targeted online data selection and rollout replay." NeurIPS, 2025.

[C] Huang, Baizhou, and Xiaojun Wan. "Pros: Towards compute-efficient rlvr via rollout prefix reuse." ICLR, 2026.

Questions for authors
  • How does RAIL differ and compare to existing learned rollout-selection methods?
  • What motivates optimizing reward-variance improvement rather than directly estimating the expected downstream policy-performance improvement induced by an intervention?
5 comments
AuthorsOpenReview ↗

Rebuttal Part - [1/5] A more comprehensive discussion and comparison would help establish the precise novelty and contribution of the proposed method.

Thank you for the references. We agree that a more comprehensive discussion and comparison is needed to establish the precise novelty of RAIL, and we will cite and discuss [A, B, C] in Appendix A, add them to Table 4 with two new dimensions (the stage at which a method acts and the quantity it learns), and restate the characterization in Section 1 and Section 2.2 in terms of what is learned. Our current comparison already includes VIP as a learned and calibrated task-level allocator, and we will broaden it to [A, B, C].

We agree that [B] and [C] are adaptive in the conventional sense because their difficulty or pass-rate estimates are updated online. However, these estimates describe the value of a task or query rather than the realized benefit of taking a particular intervention, so their selection policies do not directly correct cases in which the proxy remains high but the intervention adds little useful rollout signal. RAIL uses heuristics only for shadow-mode bootstrapping and then learns state-action intervention utilities directly from realized gains. These works help sharpen RAIL's novelty: prior methods use learned scores to select prompts, prefixes, or generated rollouts, whereas RAIL treats the rollout-generation intervention itself as the action and learns its state-conditioned marginal utility, jointly deciding whether and how to intervene.

[B] adaptively selects questions by their policy-dependent difficulty and replays recent rollouts. However, task difficulty characterizes performance under default rollout generation rather than the additional benefit of intervention: it cannot distinguish a difficult but recoverable task from an unrecoverable one, nor indicate where intervention is useful within a trajectory. RAIL addresses this by learning the action-conditional marginal gain of interventions at candidate trajectory states. VIP and TAMPO serve as related task-level comparators in Table 1; we will discuss the distinct learning target and replay mechanism of [B] in Table 4.

[C] reuses prefixes from earlier rollouts as augmented queries and adaptively prioritizes them through Bayesian pass-rate estimation, which decides which historical prefixes receive continuation compute and where rollouts start. However, it does not distinguish informativeness already present under ordinary rollout generation from the additional signal created by prefix reuse itself, so its estimated pass rate does not directly indicate whether applying the intervention is worthwhile, and it does not jointly choose a per-state branch budget and decoding regime. RAIL addresses this by learning the intervention-induced gain relative to the no-intervention baseline. [C] therefore partially handles non-stationarity, but it does not close both gaps in the specific sense defined by RAIL.

[A] is the closest in technique, as it also learns a contextual bandit online, which selects current or historical rollouts for the policy update. However, its decisions are restricted to trajectories that have already been generated: if the rollout pool contains no useful recovery path or sufficient reward variance, post-hoc selection cannot create the missing outcomes. RAIL addresses this by intervening before the rollout group is finalized. Thus, [A] optimizes which generated data the policy learns from, whereas RAIL optimizes the process that generates the learning signal. The two are complementary, since a scheduler such as [A] could be applied to the rollouts that RAIL produces.

We agree that [A, B, C] are alternative approaches to data-efficient post-training and belong in the comparison, although they differ from RAIL in decision stage, decision object, or learned target. Table 1 compares RAIL with methods that directly modify rollout generation, namely step-level branching and task-level allocation; we will make this scope explicit in Section 1.

AuthorsOpenReview ↗

Rebuttal Part - [2/5] Reward variance and the distance-based label

We thank the reviewer for raising this point, and we agree that the paper should have distinguished these quantities in the main text. We hope to clarify that Equation (2) is the general definition of recoverability, while Appendix B.3.3 is its specific implementation for the binary rewards used in all our experiments. The unregularized implementation is not a conflicting intervention criterion, but an order-preserving reparameterization of reward-variance gain. For a rollout group Y with success rate p(Y), the binary reward variance is I(Y) = 1/4 − d(Y)² with d(Y) = |p(Y) − 1/2|, so for the groups Y and Y′ before and after an intervention,

I(Y′)−I(Y)=(d(Y)−d(Y′))(d(Y)+d(Y′)).I(Y') - I(Y) = \big(d(Y) - d(Y')\big)\big(d(Y) + d(Y')\big).

The first factor is the distance reduction that we use as the label, and the second factor is never negative, so the two signals always have the same sign. When candidate interventions are compared at the same state against the same pre-intervention pool, they induce the same ordering before cost regularization. We compute the gain in this form because the shadow-mode heuristic keeps a branch by the same test (Section 3.2).

Regarding the cost term, we agree that it should have been made explicit in the main text. In the reported experiments, the label is y = d(Y) − d(Y′) − λ · C(b), where C(b) is the number of added continuations and λ = 0.005. This term does not replace recoverability as the intervention criterion; it regularizes how recoverability is used under a constrained rollout budget. It can change the ranking among interventions, and this is intended: interventions that expose similar additional reward variance should not be treated as equally desirable when they require substantially different numbers of continuations. Without it, the label would not account for the number of continuations an intervention consumes, so a larger branch budget, which has more chances to expose a differing outcome, would tend to be preferred even when a smaller budget achieves a similar gain.

As for why we use reward variance, it is not a guarantee of final performance, but a proxy for the group-relative learning signal that is observable immediately after an intervention and can be assigned to it: when all rewards in a group are equal, their centered advantages vanish (Appendix C.1). Appendix D.5 discusses this choice against a direct estimate of downstream improvement.

We will revise Section 3.1 to distinguish explicitly among (i) reward-variance recoverability, (ii) its order-preserving binary distance reparameterization, and (iii) the cost-aware controller utility used in experiments, and use the same notation in Algorithm 1.

AuthorsOpenReview ↗

Rebuttal Part - [3/5] Writing and terminology

Thank you for this suggestion. We agree that the paper is too compressed and that the coined terms make it harder to compare with existing work: "reward contrast" is the empirical reward variance of a rollout group, and "shadow-to-live" is a heuristic warm-up followed by online controller deployment, as the reviewer describes. We will replace "reward contrast" with "empirical reward variance" throughout the paper, describe the deployment procedure in standard operational terms, and replace unnecessary coined terms with standard terminology, retaining shorthand names only where they distinguish a specific operational component of the framework. In standard terms, our contributions are:

  1. an outcome-based criterion for rollout intervention based on intervention-induced improvement in empirical reward variance, instantiated in our binary-reward experiments through an cost-regularized distance-based score with a cost regularizer (Equation (2), Appendix B.3.3);
  2. an online contextual-bandit controller that learns state-intervention utilities from realized intervention outcomes, rather than selecting interventions solely from task- or query-level proxy estimates;
  3. a structured intervention space in which the controller jointly chooses the branch budget and the decoding regime.

We will state the contributions this way in Section 1.

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