acceptodds
Under review as a conference paper at ICLR 2027

Rollout-Time Intervention: Unlocking Agentic Reinforcement learning Beyond Policy Limits

Abstract

Reinforcement learning (RL) has emerged as a key paradigm for improving large language model (LLM) agents, enabling stronger reasoning, planning, and tool-use in interactive environments. However, existing agent RL methods remain fundamentally constrained by an on-policy reasoning bottleneck: when tasks exceed the model’s current capability boundary, effective trajectories become extremely sparse and training often collapses. We introduce Rollout-Time Intervention (RTI), a technique designed to elicit successful trajectories beyond the policy's intrinsic exploration capacity. RTI operates by leveraging reward-side evidence (i.e., evaluation rubrics) during rollout to convert erroneous trajectories into successful ones, providing effective learning signals for tasks that the policy rarely solves on its own. Although intervention trajectories are inherently off-policy, we find that they can effectively guide policy optimization when trajectories with excessive distributional shifts are filtered out. Extensive experiments across five benchmarks demonstrate that RTI consistently outperforms RL baselines, enabling the post-trained policy to approach the performance of substantially stronger contemporary LLMs and, more importantly, transcend its original capability boundary.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Agent, LLM

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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 addresses the failure mode of agentic RL when the task lies beyond the policy's current capability: successful trajectories are so sparse that group-relative methods receive all-zero rewards and training stalls or collapses. The proposed technique, Rollout-Time Intervention (RTI), keeps the training algorithm (GRPO) unchanged and instead intervenes during rollout generation. When an entire rollout group of G = 8 trajectories fails, a three-role multi-agent pipeline, instantiated with the policy model itself, is invoked: a Reward-Oriented Trajectory Validator judges whether the current step has critically deviated from a valid path to the gold outcome using reward-side evidence (the evaluation criteria and reference route), a Policy-Aligned Trajectory Corrector rewrites the step into a minimally corrected response that is instructed to look like a natural continuation of the policy's own reasoning while never echoing privileged information, and an Integrity-Constrained Intervention Verifier rejects corrections that leak privileged content, fabricate tool results, use tool arguments contradicting visible history, or are unreasonable.

Two further mechanisms handle the resulting off-policyness. First, a perplexity gate rescales each corrected response under the rollout prompt conditioned only on the visible history, discarding any correction whose perplexity exceeds a threshold, which is set to 5 after a sweep over 0, 3, 5, 20, and infinity. Second, reasoning-shift-aware token reweighting computes a per-token likelihood ratio between the correction prompt and the rollout prompt, clips it to a symmetric band, detaches it from the graph so it only rescales the advantage, and applies it only to tokens of intervened trajectories, so RTI reduces exactly to GRPO on groups that already succeed. An intervened trajectory replaces a single failed member of the group only if the full intervened rollout attains reward 1. Appendix B adds a convergence analysis claiming the same order-1 over square-root-K stationarity rate as clipped policy gradient, with an additive constant growing in the intervention mixing ratio. Experiments cover five settings (a self-built Navigation benchmark, tau-squared-Bench Telecom, Retail and Airline, and a 20-task Claw-Eval-Hard20 subset) with Qwen3-8B and Qwen3.5-9B backbones, comparing against the vanilla backbones, larger same-family models, contemporaneous proprietary models, GRPO, GSPO, AEPO, and the teacher-guided methods OPD and LUFFY, with ablations of the verifier, the perplexity gate, and the reweighting.

Critical strengths
  1. The core intervention idea is genuinely new and the mechanism is unusually clean where it matters. Rather than changing the optimizer, RTI keeps GRPO intact and intervenes only in rollout generation, and it does so only when the whole group fails, which means it reduces exactly to GRPO on groups the policy can already solve (Algorithm 1, step 6). That property is what makes the many claims in the paper legible: any measured difference must come from the failed groups alone, and Table 6 confirms this empirically, reporting that intervention triggers on only 15.0 percent of rollout groups in tau-squared-Telecom. The self-intervention design, in which the validator, corrector and verifier are all the policy model itself, is also attractive because it requires no external teacher, and Figure 6's finding that a stronger intervening model is actively worse is a useful and non-obvious empirical result. This is the part of the paper that made me want to recommend acceptance while reading the method section.

  2. The reported gains on the hardest settings are large, and the paper is careful to report the metrics that would expose a purely exploratory effect. The improvements are not marginal: on tau-squared-Telecom with Qwen3-8B, Pass@1 rises from 36.84 under GRPO to 61.40, and on Navigation from 35.33 to 57.33. More importantly, the paper reports the all-of-k metric, which measures consistency across repeated attempts rather than best-of-k, and RTI's advantage does not vanish there (for example 46.49 versus 21.93 on tau-squared-Telecom); a method that merely got lucky on a few rollouts would not show that pattern. The paper also reports out-of-distribution transfer on 179 Claw-Eval task families that never contributed to training-data synthesis (Table 7, Pass@1 rising from 54.34 to 62.92 over the base policy), and it reports the pre-intervention rollout pass rate rising during training (Figure 4), which is the right quantity to look at if one wants to show that intervention is not merely being consumed at rollout time.

Critical weaknesses
  1. The capability gain is produced by injecting privileged reward-side information into the rollout, and the paper never demonstrates that the resulting policy solves the evaluation tasks without that channel. In every setting the validator and corrector receive the evaluation criteria and, for Navigation, the reference route with ground-truth parameters; the Navigation validator prompt literally contains "order, ref, groundtruth", and the corrector contains "Reference/groundtruth (for calibration only; MUST NOT appear in output)". The pipeline is therefore better described as warm-starting the policy with a sequence-level hint sampled from its own conditional distribution given the answer, and the abstract's claim that RTI enables the policy to transcend its original capability boundary is exactly the claim that this hint channel does not explain the result, yet no experiment isolates it. Two things make this materially harder rather than a pedantic objection. First, the evidence that intervention is internalized is measured during training under the same privileged setup (Figure 4's pre-intervention Pass@8 and Figure 5a's falling perplexity of intervened steps under the policy), not on the held-out test sets with the channel removed. Second, the strongest comparison is near-circular in a specific way: Claw-Eval-Hard20 is scored by an LLM judge (Qwen3.7-Max) applying a rubric, the tau-squared user simulator is Qwen3.5-397B-A17B, and the policy is Qwen3.5-9B, so a judge from the same family is grading trajectories whose decisive reasoning tokens were authored under a prompt containing that same family's rubric; the Qwen3.5-9B policy reaching 85.00 Pass@1 on Claw-Eval-Hard20 exceeds even the proprietary comparisons and is precisely the kind of number that demands the hint-free control. In short, without an evaluation of the final checkpoint on the held-out test sets with intervention disabled and the reward-side evidence withheld, I cannot distinguish "the policy learned the task" from "the reported metric is largely explained by test-time privileged sampling plus rejection."

  2. The component ablations show that the intervention is, by itself, worse than the baseline, and the paper under-reports the uncertainty and the selection that surround its largest numbers. Removing only the verifier collapses RTI on tau-squared-Telecom to 38.60 Pass@1 against GRPO's 36.84, and drops it below GRPO on Navigation (26.00 versus 35.33); that means essentially all of the tau-squared-Telecom gain requires the verifier to be present, so the effect being measured is dominated by which privileged reasoning traces survive filtering, not by the correction mechanism as such. A direct control is missing and would be cheap: accept or reject intervened trajectories by a criterion unrelated to task success (for example a length or plausibility preference), then measure convergence and final success. The uncertainty reporting amplifies this: no standard deviations, confidence intervals, or seed counts appear anywhere in Tables 1, 2, 3, or 7, and several of the headline numbers come from 20-task or 150-instance evaluations where a single task is worth 5 or 0.67 points. Finally, the Claw-Eval-Hard20 training data consists of eight structure-preserving synthetic variants of each of the same 20 task families as the test set, so in-distribution generalization is being measured across near-duplicated task families, and the test set itself was difficulty-screened using the base policy, which biases both the base rate and the apparent headroom. The paper does report the Rest-OOD numbers and explicitly flags the family overlap in Appendix D.6, which is creditworthy, but the 85.00 figure in the abstract and body is the ID number.

Questions for authors

The decisive control. Please report the final checkpoint's performance on all held-out test sets with intervention fully disabled and the reward-side evidence withheld from the pipeline. Does the policy trained by RTI still exceed GRPO on Navigation, tau-squared-Telecom, and Claw-Eval-Hard20 when no hint is available at evaluation time? If the gain is confined to cases where the pipeline is available, the abstract's claim about transcending the capability boundary should be restated.

What exactly is the reward-side evidence, and who authors it? For each benchmark, is it the official task rubric, the ground-truth reference action sequence, the environment's success criterion, or something you wrote? Is the same artifact shown to the validator and the corrector for test tasks as for training tasks, and does any part of it overlap with the test grader's rubric? This determines whether the intervention is a form of self-distillation or a form of answer leakage.

Bypassing the intervention. If you instead sample exactly one additional trajectory per fully-failed group (same 8 plus 1 budget) and admit it only when the official evaluator marks it successful, how does the result compare with RTI? That baseline has the same extra sample budget but no privileged evidence and no multi-agent pipeline.

The verifier ablation. Removing the verifier makes RTI worse than GRPO on Navigation and roughly equal on tau-squared-Telecom. What acceptance rate does the verifier have, how often does the validator flag steps in trajectories that would have succeeded anyway, and does the gain survive if you match the rejection rate with a semantically neutral filter of the same strength?

Uncertainty and compute. Please give seed counts, means, and standard deviations for at least the two backbones on Navigation and tau-squared-Telecom, and report the total generation cost of RTI relative to GRPO in generated tokens and wall-clock, including validator, corrector, verifier, and rejection overhead. Section 5.4 reports that interventions deviate and are discarded, but the discarded cost is never quantified.

Is the test evaluation hint-free? Section 5.1 states that you follow the original evaluation protocols, but it is not stated whether the intervention pipeline is disabled during the final test evaluation and whether the reward-side evidence is withheld there. Please state this explicitly for each benchmark.

Table 6 interpretation. The validator flags 56.6 percent of steps in triggered groups as invalid, and 97.4 percent of intervened trajectories contain at least one accepted correction, while average tool calls drop from 0.55 to 0.31 and characters from 2045 to 1097. Is the intervention producing shorter, more efficient trajectories, or is it producing trajectories that satisfy the validator's notion of a valid path, which is the same model that authored the correction? A human or independent-judge assessment of a sample of intervened trajectories would settle this.

Concealment instruction. The corrector prompt states that reasoning must never mention or imply that it knows the correct answer, final goal, or reference behavior, and that corrections "should feel like natural evolution, not a 180-degree turn." Since this teaches the training policy to conceal knowledge it in fact possesses, did you check whether any concealment behavior persists into the final policy's behavior on held-out tasks? This matters for deployment in user-facing service domains.

tau-squared data provenance. Table 4 reports 114 training and 114 test instances for Telecom. Is the AReaL training set for tau-squared disjoint from the official tau-squared test split? If the test split is small, please also report how many distinct tasks the reported Pass@1 differences correspond to.

6 comments
AuthorsOpenReview ↗

Rebuttal to Reviewer_vBnd (1/5)

We thank the reviewer for the detailed and constructive feedback. We address each concern below.

W1.1: The capability gain is produced by injecting privileged reward-side information into the rollout, and the paper never demonstrates that ... I cannot distinguish "the policy learned the task" from "the reported metric is largely explained by test-time privileged sampling plus rejection."

Response: We thank the reviewer for raising this concern. The results in the paper's Tables 1 and 2 already evaluate the checkpoints with RTI disabled. Privileged reward-side information is used only during training to correct failed rollouts. At test time, all policies generate trajectories under the same evaluation protocol, without intervention or access to privileged information. We will make this distinction explicit in Section 5.1.

W1.2: Second, the strongest comparison is near-circular in a specific way: Claw-Eval-Hard20 is scored by an LLM judge (Qwen3.7-Max) applying a rubric, ... the Qwen3.5-9B policy reaching 85.00 Pass@1 on Claw-Eval-Hard20 exceeds even the proprietary comparisons and is precisely the kind of number that demands the hint-free control.

Response: On τ2\tau^2-Bench, deterministic benchmark checks determine task success based primarily on the final environment state and additional task-specific assertions. No LLM judge assigns success labels. On Claw-Eval-Hard20, we re-scored the same evaluation trajectories with DeepSeek-V4.1-Flash using the same rubric and scoring protocol. RTI ranks first on all three metrics under both judges, and GRPO’s aggregate scores are identical across judges. Across the trajectories, the judges’ scores have a Spearman correlation of 0.983 and a Kendall correlation of 0.930. RTI’s lead thus persists with a judge from a different model family.

Table 1. Judge robustness on Claw-Eval-Hard20. GRPO and RTI use Qwen3.5-9B checkpoints. All scores are percentages.

MethodQwen3.7-Max p@1avg p@kavg p^kDeepSeek-V4.1-Flash p@1avg p@kavg p^k
GRPO52.5057.7145.4252.5057.7145.42
RTI85.0094.1773.9686.2594.4877.08
Claude-4.6-Sonnet51.2559.2744.1747.5051.9843.02
AuthorsOpenReview ↗

Rebuttal to Reviewer_vBnd (2/5)

W2.1: The component ablations show that the intervention is, by itself, worse than the baseline ... so the effect being measured is dominated by which privileged reasoning traces survive filtering, not by the correction mechanism as such.

Response: We agree that the Verifier is a key component of RTI. Without it, corrected trajectories may contain actions that rely on privileged information unavailable to the policy, making them unsuitable as training examples. The Corrector and Verifier serve complementary roles. The Corrector proposes candidate revisions to failed rollouts, and the Verifier screens those revisions for issues such as information leakage. The ablation shows that verification is important for turning corrections into useful training data.

W2.2: A direct control is missing and would be cheap: accept or reject intervened trajectories by a criterion unrelated to task success (for example a length or plausibility preference), then measure convergence and final success.

Response: We replaced the Verifier with a random filter that rejects 50% of corrected steps independently of task success. Random filtering improves over removing the Verifier on both benchmarks (τ2\tau^2-Telecom Pass@1: 38.60 →\rightarrow 43.45; Navigation: 26.00 →\rightarrow 33.33). Full RTI nevertheless outperforms the random-filter variant on all three metrics across both benchmarks, suggesting that the Verifier’s acceptance criteria matter beyond simply reducing the number of corrections used for training.

Table 2. Random-filter control on Qwen3-8B. All intervention variants share the same Validator and Corrector.

VariantNavigationτ2\tau^2-Telecom
p@1avg p@kavg p^kp@1avg p@kavg p^k
GRPO (no intervention)35.3340.0029.0036.8455.4821.71
RTI w/o Post-Check26.0033.3314.1738.6054.8223.68
RTI w/ random filter (50% rejected)33.3348.0023.3343.4557.6124.92
RTI57.3362.3346.6761.4081.1444.30

W2.3: The uncertainty reporting amplifies this: no standard deviations, confidence intervals, or seed counts appear anywhere in Tables 1, 2, 3, or 7, and several of the headline numbers come from 20-task or 150-instance evaluations where a single task is worth 5 or 0.67 points.

Response: As in the paper, we evaluate each checkpoint four times. Table 3 reports the mean and standard deviation of p@1 across these four evaluations. The standard deviations quantify rollout sampling variability at evaluation time for each fixed checkpoint.

Table 3: Mean ±\pm std of p@1 over four repeated evaluations on Navigation and τ2\tau^2-Telecom (percentages; cell = mean ±\pm std of p@1).

MethodNavigation (Qwen3-8B)Navigation (Qwen3.5-9B)τ2\tau^2-Telecom (Qwen3-8B)τ2\tau^2-Telecom (Qwen3.5-9B)Claw-Eval-Hard20 (Qwen3-8B)Claw-Eval-Hard20 (Qwen3.5-9B)
GRPO35.33 ±\pm 1.5971.33 ±\pm 0.6436.84 ±\pm 2.8195.61 ±\pm 1.14322.50 ±\pm 7.5052.50 ±\pm 5.00
RTI57.33 ±\pm 2.3174.67 ±\pm 1.6361.40 ±\pm 4.2196.49 ±\pm 1.26450.00 ±\pm 7.0785.00 ±\pm 4.08

W2.4: Finally, the Claw-Eval-Hard20 training data consists of eight structure-preserving synthetic variants of each of the same 20 task families as the test set, ... but the 85.00 figure in the abstract and body is the ID number.

Response: Thank you for this suggestion. In the revision, we will identify the 85.00 p@1 result as in-distribution and move the Rest-OOD results from Appendix D.6 to the main text.

AuthorsOpenReview ↗

Rebuttal to Reviewer_vBnd (3/5)

Q1: The decisive control. Please report the final checkpoint's performance on all held-out test sets with intervention fully disabled ... If the gain is confined to cases where the pipeline is available, the abstract's claim about transcending the capability boundary should be restated.

Response: Yes. As clarified in W1.1, the paper's Tables 1 and 2 already report the checkpoints’ performance with intervention fully disabled and privileged reward-side information withheld from the policy. We will make this protocol explicit in Section 5.1.

Q2: What exactly is the reward-side evidence, and who authors it? ... does any part of it overlap with the test grader's rubric? This determines whether the intervention is a form of self-distillation or a form of answer leakage.

Response: RTI uses the same task-specific information that GRPO’s reward function uses to score training rollouts. RTI also uses that information to guide corrections during training. Specifically, it consists of the task completion criteria and required actions from AReaL for τ2\tau^2-Bench, the reference direction arguments and waypoint order constraints for Navigation, and the rubrics created during data synthesis to score the synthetic Claw-Eval training instances. Appendix A.1 shows the intervention prompts for τ2\tau^2-Bench and Navigation.

At test time, the intervention pipeline is disabled. The test references and rubrics, including the official Claw-Eval rubrics, are used only to score completed trajectories.

Q3: Bypassing the intervention. If you instead sample exactly one additional trajectory per fully-failed group (same 8 plus 1 budget) ... how does the result compare with RTI?

Response: We evaluated three alternatives to intervention on τ2\tau^2-Telecom and Claw-Eval-Hard20.

  1. 8+1 resampling. For each fully failed group of eight, sample one additional trajectory and retain it only if the benchmark evaluator assigns a reward of 1.
  2. Larger rollout group. Increase the rollout group size from 8 to 16.
  3. DAPO-style resampling. Keep the group size at 8 and continue sampling until at least one trajectory succeeds.

The 8+1 control improves p@1 over GRPO by about 1.3 percentage points on each benchmark. The best resampling variant reaches 39.21 and 58.08 p@1, respectively, compared with 61.40 and 85.00 for RTI. These results suggest that additional on-policy sampling provides limited gains when successful trajectories are rare.

Table 4. Sampling alternatives to intervention on τ2\tau^2-Telecom (Qwen3-8B).

VariantSampling per groupp@1avg p@kavg p^k
GRPO836.8455.4821.71
8+1 resampling8 + 1 if all fail38.1358.6321.22
Larger rollout group1638.6056.1422.37
DAPO-style resampling8 + resampling39.2157.3725.72
RTI8 + intervention if all fail61.4081.1444.30

Table 5. Sampling alternatives to intervention on Claw-Eval-Hard20 (Qwen3.5-9B).

VariantSampling per groupp@1avg p@kavg p^k
GRPO852.5057.7145.42
8+1 resampling8 + 1 if all fail53.7566.7741.67
Larger rollout group1655.0067.2942.71
DAPO-style resampling8 + resampling58.0867.1646.92
RTI8 + intervention if all fail85.0094.1773.96
Reviewer_WmZfOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper tackles the on-policy reasoning bottleneck with a multi-agent structure, restoring the learning signal by correcting responses on “all-zero” samples. The proposed RTI method uses a validator to locate the critical error step, a corrector to fix the error and suggest a correct answer, and a verifier to assess the quality of the corrected answer for filtering. In addition, a gating mechanism and a reweighting mechanism further filter the corrected answers and adjust their token weights.

Critical strengths

The problem is well identified and the method is carefully designed, but I think the paper still needs some further ablations to be complete.

Critical weaknesses
  1. What is the fraction of the “all-zero” samples in the training set? If this fraction were raised or lowered, how would the method’s performance change?
  2. Does the corrector revise all of the rollouts for a group, or only one?
  3. Are there samples where the correction fails, i.e., where everything is filtered out by the later stages? Is the corrector robust across problems of different difficulty?
  4. What are the training resource requirements after introducing the multi-agent setup?
Questions for authors

See weaknesses above.

1 comment
AuthorsOpenReview ↗

Rebuttal to Reviewer_WmZf

We thank the reviewer for the detailed and constructive feedback. We address each concern below.

W1: What is the fraction of the "all-zero" samples in the training set? If this fraction were raised or lowered, how would the method's performance change?

Response: We trained Qwen3-8B with GRPO on each dataset and counted all-zero rollout groups during the first pass through the training data, before convergence. A group is all-zero if all eight rollouts receive zero reward. The denominators in Table 1 are the total numbers of rollout groups observed during that pass on each dataset.

Table 1. All-zero rollout groups during the first pass of GRPO training.

DatasetAll-zero groups / total groupsFraction of all-zero groups
τ2\tau^2-Telecom131 / 27248.16%
Navigation337 / 53662.87%

The fraction arises from the policy’s rollout outcomes on each dataset. Navigation has a higher all-zero fraction and a lower final RTI Pass@1 than τ2\tau^2-Telecom. Estimating the effect of changing this fraction would require a controlled comparison within the same dataset.

W2: Does the corrector revise all of the rollouts for a group, or only one?

Response: The Corrector attempts to revise all rollouts in an all-zero group. If any revised rollout succeeds, we randomly select one of the successful revisions to replace a failed rollout in the group.

W3: Are there samples where the correction fails, i.e., where everything is filtered out by the later stages? Is the corrector robust across problems of different difficulty?

Response:

a. Correction failures. Yes. A correction attempt fails at the group level if no revised rollout both passes the subsequent filters and succeeds. We revised Appendix Table 6 to account for corrections removed by the perplexity gate. On τ2\tau^2-Telecom with Qwen3-8B, the gate removed 705 of the 5,166 corrections accepted by the Verifier (13.65%). After filtering, 1,122 of the 1,200 intervened rollouts retained at least one correction, while 78 (6.50%) retained none.

Table 2: Intervention funnel behind the statistics of the paper's Table 6 (τ2\tau^2-Telecom, Qwen3-8B).

LevelStageCountRatio
GroupRollout groups sampled per iteration1,000--
Groups with intervention triggered (all-failure groups)15015.00% of groups
RolloutIntervened rollouts generated (8 per triggered group)1,2008 per triggered group
StepSteps inside intervened rollouts15,44012.87 per rollout
Steps flagged invalid by the Validator8,73956.60% of steps
Corrections accepted by the Verifier5,16659.11% of flagged steps
Corrections rejected by the Verifier3,57340.89% of flagged steps
Corrections passing the perplexity gate4,461705 of 5,166 rejected (13.65%)
TrajectoryIntervened rollouts with ≥1\geq 1 retained correction1,12293.50%
Retained corrections per such trajectory3.98--

b. Performance across task difficulty. We grouped Claw-Eval-Hard20 task families by the number of times Claude-4.6-Sonnet solved the original task in four trials, using this count as a proxy for difficulty. Group-level correction success was 83.82% in the hardest tier (0/4) and 94.12–100.00% in the other tiers. These results suggest that the correction pipeline is robust across the difficulty levels tested, although failures are more frequent in the hardest tier.

Table 3. Group-level correction success on Claw-Eval-Hard20 (Qwen3.5-9B), grouped by Claude-4.6-Sonnet’s pass count over four trials.

Claude passesGroups requiring correctionSuccessfully corrected groupsGroup success rate
0/4 (hardest)685783.82%
1/42525100.00%
2/4171694.12%
3/488100.00%
4/4 (easiest)2121100.00%
Total13912791.37%

W4: What are the training resource requirements after introducing the multi-agent setup?

Response: RTI runs on the 8×NVIDIA H20 GPU as GRPO. The Validator, Corrector, and Verifier all reuse the policy model, so the multi-agent setup requires no additional accelerators or separately deployed models. The intervention does add inference calls during training.

Reviewer_vBndOpenReview ↗
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2
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2
Informativeness
2
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Paper summary

RTI addresses all-failure rollout groups in agent RL, where GRPO gets no reward learning signal. The policy uses training-side rubrics and target actions to check, correct, and verify steps, then puts successful trajectories back into the training group. The paper reports large gains on Navigation, τ²-Bench, and Claw-Eval, including transfer to tasks not used for training-data synthesis.

Critical strengths
  1. The problem is practical and the gains are large. Hard20 improves from 22.50 to 50.00 for Qwen3-8B and from 52.50 to 85.00 for 9B over GRPO (Tables 1–2). Intervention uses the policy itself by default.

  2. The gains carry over to evaluation without intervention. On the 179 Rest-OOD tasks, RTI scores 62.92 versus 56.56 for GRPO (Table 7). Table 3 also shows that the filters matter.

Critical weaknesses
  1. What does the three-role pipeline add over simple hint-guided rollouts? Guide-GRPO and ExPO already use hints or answers to produce learnable positive samples, but neither is discussed. RTI gets instance-level rubrics, target actions, and arguments; the teacher baselines do not get the same information. This leaves extra supervision and local correction confounded. The key control is the same policy rerolling with the same rubric, with similar filtering and compute. The Validator also lacks an accuracy check or ablation. It flags 56.6% of steps in intervened trajectories (Table 6), so correction may be less local than the motivation suggests. That does not establish false positives, but it needs explanation. The results support not needing a stronger intervention model, rather than the broader comparison with teacher-limited methods.

  2. The sampling protocols need clarification before I can judge the teacher comparison. Appendix C.3 says LUFFY replaces the failed group with successful teacher trajectories. If the whole group becomes successful, its reward advantages are zero; original LUFFY mixes on-policy and off-policy trajectories. This may just be imprecise wording. For RTI, Algorithm 1 adds one rollout per triggered group, but Table 6 lists 150 groups and 1,200 intervened trajectories. Its 97.42% counts trajectories with an accepted correction, not final successes used in training. How much successful data and extra compute does RTI actually add? Checkpoint and threshold selection are also unclear.

Questions for authors
  1. Can you compare with simple rerolling under the same rubric and a similar budget? A clear RTI advantage would strengthen the local-intervention contribution; otherwise, please narrow the capability-boundary claims.

  2. How many teacher and on-policy trajectories does LUFFY mix, and is policy shaping retained? Why do RTI's 150 groups produce 1,200 trajectories, and how many enter training? Please also give extra call counts and the data used to select checkpoints and thresholds.

  3. Have you audited Validator false positives and false negatives? Please provide the Hard20 prompts and explain how corrected facts and arguments are checked against visible history for privileged-information leakage.

  4. In Eq. (7), is the old-policy probability for corrected tokens computed under the rollout or correction prompt? Does Figure 7's 0–16 scale show raw ratios or actual training weights?

8 comments
AuthorsOpenReview ↗

Rebuttal to Reviewer_vBnd (1/5)

We thank the reviewer for the detailed and constructive feedback. We address each concern below.

W1: The contribution beyond existing hint- or answer-guided methods is not isolated ... Using training-side hints to obtain successful trajectories and then training a hint-free policy has clear precedents. Guide-GRPO (Nath et al., 2025, arXiv:2506.13923) adds hint-conditioned rollouts when all unguided rollouts for a prompt fail, and adjusts the importance ratio to optimize the policy for the hint-free context. ExPO (Zhou et al., 2025, arXiv:2507.02834) conditions on the ground-truth answer so that the model generates its own explanations as positive samples closer to the policy distribution, and reports that such samples are easier to learn from than expert demonstrations. Both predate this submission and are not discussed.

Response: We thank the reviewer for pointing out ExPO and Guide-GRPO. Both are relevant precedents for using training-time guidance to improve a policy that runs without hints at test time. We will discuss both in the revision. Their use of guidance at the trajectory level introduces different limitations when adapted to multi-turn agent tasks.

  1. ExPO uses ground-truth answers to generate demonstrations and interleaves supervised updates on those demonstrations with RL. In a long-horizon agent task, imitating a full demonstration can reinforce many decisions beyond the step that caused the failure. This can make the policy overfit to the demonstrated action sequences and limit exploration. RTI corrects the steps that caused the failure and uses the resulting trajectory directly in the RL update.
  2. Guide-GRPO uses a predefined hint to generate an additional rollout when all unguided rollouts fail. A predefined hint cannot adapt to the specific failure that occurs during an interaction. Because it is included in the initial prompt, it shifts the conditioning context for every subsequent decision in the rollout. RTI diagnoses failures from the interaction history as they occur and edits only the steps that need correction, limiting the distribution shift introduced by the intervention.

We reimplemented both baselines using the same rollout budget and final-reward as RTI. RTI outperforms both on all reported metrics. These results support the effectiveness of step-level correction in the multi-turn settings tested.

Table 1. Comparison on τ2\tau^2-Telecom (Qwen3-8B). Scores are percentages, with k=1,…,4k=1,\ldots,4.

Methodp@1avg p@kavg p^k
GRPO36.8455.4821.71
ExPO42.1158.7725.22
Guide-GRPO50.0065.7928.07
RTI61.4081.1444.30

Table 2. Comparison on Claw-Eval-Hard20 (Qwen3.5-9B). Scores are percentages, with k=1,…,4k=1,\ldots,4.

Methodp@1avg p@kavg p^k
GRPO52.5057.7145.42
ExPO57.5066.2545.00
Guide-GRPO67.5084.2750.73
RTI85.0094.1773.96
AuthorsOpenReview ↗

Rebuttal to Reviewer_vBnd (2/5)

W2: The Validator, which localizes errors step by step, is the component that most distinguishes RTI from these method ... Still, if the Validator is unreliable, the case for step-level local correction over plain guidance becomes weaker.

Response:

a. Motivation for the Validator. As Figure 1 illustrates, one or two critical errors can cause an entire agent trajectory to fail. We therefore aim to correct only those steps and let the agent complete most of the trajectory on its own. This keeps the corrected trajectory close to what the policy can already produce, making it easier for the policy to learn the correction gradually. A separate Validator determines which steps need correction and avoids unnecessary Corrector calls. When the two components are merged, the model may be more inclined to rewrite steps that were already valid. This adds correction overhead and can produce trajectories that are farther from the policy’s own rollout distribution.

b. Validator inputs. The Validator receives the evaluation criteria in its prompt. These criteria describe what must eventually be satisfied for the task to succeed, helping the Validator judge whether the current step keeps the trajectory on track. For Navigation and τ2\tau^2-Telecom, tasks within each benchmark share a common set of criteria, which we show in the prompts in Appendix A.1. For Claw-Eval-Hard20, tasks vary, so the Validator receives the rubric used to score each synthetic training instance. This is why we did not show a single shared set of criteria for Claw-Eval-Hard20.

c. Validator accuracy. We used DeepSeek-V4.1-Flash to annotate whether each of 461 steps from τ2\tau^2-Telecom trajectories generated by Qwen3-8B required correction. The Validator achieved 86.79% precision and 85.87% recall. Thus, 86.79% of the steps flagged by the Validator were judged to require correction.

Table 3. Step-level Validator accuracy on annotated τ2\tau^2-Telecom trajectories (Qwen3-8B).

BenchmarkStepsPrecisionRecallF1
τ2\tau^2-Telecom46186.79%85.87%86.32%

d. Validator ablation. On Claw-Eval-Hard20 with Qwen3.5-9B, we compared RTI with a variant that merges the Validator and Corrector. In addition to task performance, we measured the fraction of steps corrected and the fraction of proposed corrections accepted. The merged variant corrected more steps, but a larger fraction of its corrections was rejected.

Table 4. Ablation merging the Validator and Corrector on Claw-Eval-Hard20 (Qwen3.5-9B). All values are percentages.

Variantp@1avg p@kavg p^kCalibrated steps / total stepsAccepted / produced corrections
RTI85.0094.1773.96855 / 3,384855 / 1,174
RTI w/ merged Validator+Corrector77.5092.4058.851025 / 3710347 / 1025

W3: The current comparisons cannot separate two explanations: the gains come mainly from turning instance-level evaluation information ... If the two are close, the contribution is better described as an implementation and empirical study of hint-guided self-training for multi-turn agent tasks.

Response: Thank you for suggesting this control. In addition to ExPO and Guide-GRPO, we evaluated a sequence-level variant that gives the same policy access to the same instance-level evaluation information as RTI. When all rollouts in a group fail, the policy uses that information to regenerate a full trajectory. The regenerated trajectory is eligible to replace a failed rollout only if it succeeds and passes the same Verifier and perplexity gate as RTI. The policy is then trained in the original hint-free context.

Sequence-level guidance improves over GRPO on both benchmarks. With the same evaluation information, step-level RTI further improves p@1 by 14.54 percentage points on τ2\tau^2-Telecom and 8.75 points on Claw-Eval-Hard20. One explanation is that conditioning the entire rollout on the evaluation criteria shifts the policy’s generation context from the first turn, whereas local correction limits direct intervention to the steps identified as needing revision. These results support the added value of step-level diagnosis and correction under the same training-time supervision.

Table 5. Equal-information control on τ2\tau^2-Telecom (Qwen3-8B). All scores are percentages.

Variantp@1avg p@kavg p^k
GRPO36.8455.4821.71
RTI (sequence-level)46.8666.5427.94
RTI61.4081.1444.30

Table 6. Equal-information control on Claw-Eval-Hard20 (Qwen3.5-9B). All scores are percentages.

Variantp@1avg p@kavg p^k
GRPO52.5057.7145.42
RTI (sequence-level)76.2584.4867.08
RTI85.0094.1773.96
AuthorsOpenReview ↗

Rebuttal to Reviewer_vBnd (3/5)

W4: The comparison with teacher-guided baselines and RTI's own sampling protocol are ambiguous in ways that affect the main conclusions. ... so the actual implementation needs to be confirmed.

Response: The wording in Appendix C.3 was imprecise. In our LUFFY implementation, we replace one rollout in an all-failure group with a successful trajectory generated by the stronger teacher on the same task. The resulting group contains seven on-policy rollouts and one off-policy teacher trajectory, consistent with the original LUFFY setup.

W5: RTI's own protocol also needs clarification. Algorithm 1 and Appendix A.2 say that each triggered group gets one intervened rollout ... the paper does not state how checkpoints were chosen for each method.

Response: Intervention protocol and the paper's Table 6. Algorithm 1 and Appendix A.2 use “one intervened rollout” to refer to one intervention batch per triggered group. For each triggered group, RTI generates eight additional rollouts, matching the original group size, and uses privileged information to propose corrections at the current step. Thus, the 150 triggered groups in the paper's Table 6 yielded 1,200 intervened rollouts. If an intervened rollout succeeds, at most one successful rollout replaces a failed trajectory in the original group.

We revise the reported trajectory-level rate from 97.42% to 93.50% (1,122 of 1,200). The original calculation counted Verifier acceptance alone. The revised rate measures the fraction of rollouts with at least one correction that was accepted by the Verifier and passed the perplexity gate. Table 7 reports the counts at each stage through correction retention. The reward-1 success rate and the fraction of intervened rollouts admitted to the policy update remain unreported in this table.

a.LUFFY comparison. In our LUFFY implementation, one successful off-policy trajectory replaces one failed on-policy rollout, and the remaining failed on-policy rollouts are retained. We omit policy shaping in this implementation.

b.Checkpoint selection. For each training method, including GRPO, we report the highest test-set score observed across evaluated training checkpoints. The GRPO score of 52.50 reported in the paper's Table 2 was selected using this same rule. Figures 4 and 6 also show performance over training. RTI generally remains above the corresponding baselines in the later stages of training.

c.Perplexity threshold. Figure 3 shows results on the Navigation test set. We selected the perplexity threshold δppl=5\delta_{\mathrm{ppl}} = 5 using these test-set curves.

Table 7: Intervention funnel behind the statistics of the paper's Table 6 (τ2\tau^2-Telecom, Qwen3-8B).

LevelStageCountRatio
GroupRollout groups sampled per iteration1,000--
Groups with intervention triggered (all-failure groups)15015.00% of groups
RolloutIntervened rollouts generated (8 per triggered group)1,2008 per triggered group
StepSteps inside intervened rollouts15,44012.87 per rollout
Steps flagged invalid by the Validator8,73956.60% of steps
Corrections accepted by the Verifier5,16659.11% of flagged steps
Corrections rejected by the Verifier3,57340.89% of flagged steps
Corrections passing the perplexity gate4,461705 of 5,166 rejected (13.65%)
TrajectoryIntervened rollouts with ≥1\geq 1 retained correction1,12293.50%
Retained corrections per such trajectory3.98--

Comments on the paper

1 comment

Dear AC and Reviewers,

We sincerely appreciate the time and effort that you and the reviewers have devoted to evaluating our submission and considering our rebuttal. Every clarification and every additional result requested by the reviewers is contained in the three point-by-point responses (rebuttal to Reviewer AAje, to Reviewer vBnd, and to Reviewer WmZf), where each weakness and each question is answered separately. Most of the supplementary experiments there are validation studies of analyses already in the paper rather than new components of the main experiments.

Overall, the reviewers found the problem practical and the mechanism clean, highlighting the value of converting reward-side evidence into learnable trajectories and the evidence that the gains survive without intervention.

On the problem and the intervention design:

Reviewer AAje: "The core intervention idea is genuinely new and the mechanism is unusually clean where it matters."
Reviewer vBnd: "The problem is practical and the gains are large."
Reviewer WmZf: "The problem is well identified and the method is carefully designed."

On the evidence that the policy learns rather than consuming the intervention:

Reviewer vBnd: "The gains carry over to evaluation without intervention. On the 179 Rest-OOD tasks, RTI scores 62.92 versus 56.56 for GRPO."
Reviewer AAje: "the paper reports the pre-intervention rollout pass rate rising during training (Figure 4), which is the right quantity to look at if one wants to show that intervention is not merely being consumed at rollout time."
Reviewer AAje: "a method that merely got lucky on a few rollouts would not show that pattern."

The remaining concerns fall into three groups: how RTI differs from hint-guided methods; what the fine-grained ablations of the mechanism show; and how reliable each module is in operation.

Relation to hint-guided methods. The rebuttal adds both the distinction and the experiment on ExPO and Guide-GRPO. Both baselines are trajectory-level methods built for single-turn tasks: ExPO conditions on the answer and Guide-GRPO inserts a predefined hint into the prompt of an extra rollout, so the hint fixes the conditioning context from the first turn and the resulting trajectory drifts away from the policy's own distribution. RTI instead locates the failing step from the interaction history and edits only that step, which keeps the correction inside what the policy can learn. Reimplemented under the same budget and reward, both baselines remain clearly below RTI (vBnd, Tables 1 and 2).

Fine-grained ablations. The paper already ablates the Verifier, the perplexity gate, and the reweighting (the paper's Table 3), which shows that filtering is necessary rather than auxiliary. The rebuttal adds three controls. A sequence-level variant gives the policy the same evidence and the same filters but regenerates the whole trajectory, and step-level correction still leads (vBnd, Tables 5 and 6). Merging the Validator into the Corrector rewrites more steps and performs worse (vBnd, Table 4). A random filter matched in rejection rate but unrelated to task success does not recover the gain (AAje, Table 2).

Reliability of each module. The paper reports the intervention statistics (the paper's Appendix Table 6); the rebuttal audits each module in operation. Independent annotation confirms the Validator's step-level judgments and shows its flag rate falling as the policy improves, so it is not a fixed hand-written filter (vBnd, Tables 3 and 8). The Verifier is checked by its acceptance rate and by a leakage audit, which shows that unsupported facts and arguments are largely removed after verification (vBnd, Table 9). The pipeline statistics are completed to a full funnel from triggered groups to retained corrections, and correction success is stable across task difficulties and all-zero rates (vBnd, Table 7; WmZf, Tables 1 and 3).

During the discussion, Reviewer vBnd replaced the entire review, consolidating the weaknesses and reformulating the questions, and we answered that revised version in full as well. Reviewer AAje has not posted any follow-up, although both of their critical weaknesses and all nine of their questions are answered in our response. Reviewer WmZf's current assessment is a weak acceptance. We respectfully ask the AC to weigh these responses when reaching a decision.

Thank you again for your time, your support, and your careful evaluation of our work.

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

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