acceptodds
Withdrawn from ICLR 2027

RESETTLE: Robotic Recovery through Disagreement-Triggered Retrieval and Efficient Corrective Control

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Reliable robotic manipulation requires timely intervention to correct emerging deviations and restore progress after execution errors. However, recovery methods based on repeated vision-language reasoning or iterative online optimization can incur substantial latency, delaying intervention. To address these challenges, we introduce RESETTLE (Robotic recovery through disagreement-Triggered retrieval and Efficient Corrective Control), a model-agnostic framework that provides computationally efficient recovery at the action-execution interface of frozen robot policies. RESETTLE triggers recovery when two action proposals independently sampled under identical conditioning persistently disagree. It retrieves a same-task demonstration reference using an adapted V-JEPA encoder and combines a state-servo prior with a guarded visual residual to execute one corrective action without online trajectory optimization or additional vision-language reasoning, then returns control to the base policy. Across six base policies in simulation, RESETTLE achieves up to 8.70%, 6.28%, and 6.83% absolute success-rate gains on LIBERO-Plus, Meta-World, and RoboCasa Tabletop, respectively, with further improvements on four real-world tasks using two policies. In QwenPI-based comparisons, its monitoring-and-recovery computation latency is 74.04%–93.57% lower than VoLoAgent's monitoring-and-planning latency for grasp and place tool calls. It also raises Harness VLA's LIBERO-Pro Swap success from 42% to 50%, demonstrating compatibility with high-level agentic planning.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Robot Policy Recovery, Vision-Language-Action Models, World-Action Models, Uncertainty-Aware Control, Retrieval-Guided Control

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_tz8NOpenReview ↗
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Paper summary

The paper proposes RESETTLE, an add-on recovery layer for frozen VLA/world-action policies. It samples two action chunks under identical conditioning and flags trouble when their disagreement exceeds a training-data P95 threshold at two consecutive decisions. It then retrieves the nearest same-task demonstration frame with a V-JEPA-2-AC encoder fine-tuned on demonstrations. One corrective action is built from a state-servo prior plus a guarded visual residual, and control returns to the base policy. Evaluation covers six base policies on LIBERO-Plus, Meta-World, and RoboCasa Tabletop, plus LIBERO-Pro Swap with a GPT-5.5 planner and four real-world tasks with two policies. Reported gains range from about 2 to 9 points. The paper also reports 74–93% lower monitor-plus-recovery computation than VoLoAgent, and lower than Agentic Robot and an adapted LPB.

Critical strengths
  1. The method is simple, needs no base-policy fine-tuning, and works across many policies and benchmarks, including a real robot and a planner-based system. Consistent gains of a few points across this breadth suggest a practical plug-in, which is what pushes me toward acceptance.

  2. The analysis is candid and useful. Disagreement separates failed from successful trajectories much better than V-JEPA feature distance. The paper also reports how rarely recovery actually takes over and includes explicit failure cases. This makes the claims easier to trust and interpret.

Critical weaknesses
  1. The statistical evidence is thin: Meta-World uses 10 episodes per task, LIBERO-Pro Swap 100 trials, and the real-world tests 20 trials per task, with no seeds, confidence intervals, or significance tests, so several gains (e.g., +2.09 on LDA) could be noise. The recovery module is also trained on benchmark demonstrations that the frozen baseline never sees, and there is no control such as random-trigger recovery or a small fine-tuned corrector to isolate the benefit of the trigger and retrieval.

  2. The latency comparison is not like-for-like: competing methods are re-implemented or adapted (LPB), produce different outputs (a trajectory versus one action), and totals exclude nominal inference and execution, with no end-to-end or equal-wall-clock success comparison. The "lightweight" framing also sits uneasily with a ~1B-parameter encoder plus nearest-neighbor search over the full demonstration bank. Disagreement further misses the consistent-but-wrong failures the paper itself shows.

Questions for authors
  1. Can you provide confidence intervals or multiple evaluation seeds, especially for Meta-World, LDA/RoboCasa, and LIBERO-Pro Swap? Which gains survive?
  2. Can you add controls that isolate the benefit of the trigger from the benefit of the corrective action, e.g., triggering at random with the same intervention frequency, or always-on recovery?
  3. How does a fine-tuned or DAgger-style baseline trained on the same demonstrations compare? The recovery module sees demonstration data the baseline does not.
  4. What are the memory and retrieval costs as the reference bank grows (e.g., for Meta-World's 204k frames), and how does retrieval time scale?
  5. Does the P95 threshold generalize when the test distribution differs sharply from training? Is any per-benchmark tuning of thresholds or guard parameters done?
2 comments

Thank you for recognizing the simplicity, broad applicability, and candid failure analysis of our method. We address the concerns about statistical reliability, trigger selection, and computational cost below.

1. Multiple seeds and statistical reliability

We completed evaluations with five different random seeds for both the baseline and RESETTLE. The table reports mean success rates (%) ± sample standard deviation across the five runs.

BenchmarkBase PolicyBaselineRESETTLEMean Gain (pp)
Meta-WorldQwenPI60.8 ± 1.166.3 ± 0.6+5.5
Meta-WorldSmolVLA59.8 ± 1.366.0 ± 1.2+6.1
RoboCasaLDA49.9 ± 0.852.6 ± 0.5+2.8
RoboCasaQwenGR00T53.5 ± 0.560.7 ± 0.7+7.2
LIBERO-Pro Swapπ₀.₅14.8 ± 1.524.4 ± 1.1+9.6
LIBERO-Pro SwapGPT-5.5 + π₀.₅42.2 ± 1.950.0 ± 1.2+7.8

Meta-World uses the same averaging convention over the four difficulty groups as the paper. The reported uncertainty is standard deviation. All six comparisons show positive gains in all five runs. Notably, the LDA/RoboCasa improvement remains consistent, with a mean gain of 2.8 percentage points and individual-run gains of 2.1–4.3 points. These additional results support the repeatability of the improvements across evaluation seeds.

2. Separating trigger selection from corrective actions

We added random triggering on LIBERO Plus with QwenPI, keeping retrieval and recovery fixed. H denotes the predicted action-chunk length, and K denotes the number of actions executed before re-observation and replanning during nominal execution.

TriggerH8/K4 Success (%)Mean Recoveries/TrajectoryH16/K8 Success (%)Mean Recoveries/Trajectory
Our disagreement trigger76.63.96778.92.557
Random triggering75.13.96477.52.554
No recovery73.8075.80

Under H8/K4, random recovery improves success over no recovery by 1.3 percentage points, while our trigger provides a further 1.5-point improvement at nearly identical intervention frequency. This supports the additional value of selecting when to intervene. Under H16/K8, our trigger also achieves higher success.

3. Demonstration access

We clarify that our recovery module uses demonstrations from the same training dataset used to train the base policy; it receives no additional demonstrations. Both recovery training and reference-library construction use existing training data, without additional expert corrections or DAgger-style data collection. The distinction is therefore how the demonstrations are used, rather than access to additional demonstration data.

4. Reference-library memory and retrieval costs

Default retrieval searches only same-task candidates, rather than the entire library. Measurements on LIBERO Plus are:

Demonstrations per TaskTotal FramesMean Same-task CandidatesFeature + State Memory (CPU)Mean Search Time
16,61116535.68 MiB0.085 ms
213,28733271.72 MiB0.176 ms
426,559664143.36 MiB0.406 ms
853,3231,333287.83 MiB0.866 ms
20133,7603,344722.01 MiB2.751 ms
Up to 32212,8245,3211,148.78 MiB9.227 ms
All273,4656,8371,476.11 MiB15.621 ms

For Meta-World, the library contains 204,806 frames, averaging 4,180 same-task candidates. Features and states occupy 1,103.16 MiB, the CPU memory increase after loading is 1.08 GiB, and median retrieval latency is 2.54 ms. Memory grows approximately linearly with total frame count. Search latency increases with same-task candidate count, with a steeper increase for larger LIBERO Plus libraries.

We also agree that “lightweight” characterization should refer to measured online computation and sparse intervention, rather than a small encoder parameter count.

5. Threshold generalization and selection

Our reported thresholds are calibrated at P95 using offline inference on training data, without tuning on test outcomes. For each base policy on LIBERO Plus, one threshold is shared across all variants, tasks, and suites. Appendix Table 12 reports the following QwenPI sensitivity analysis:

Different variants favor different thresholds: Robot performs best at P85, whereas Noise performs best at P99. We do not select the best threshold per variant; all main results use the training-derived P95 setting. All four percentiles improve overall success, supporting robustness to threshold choice under the evaluated shifts.

Finally, we acknowledge that consistently incorrect behavior can evade disagreement detection. Our supplementary analysis found that 146 of 1,859 failed QwenPI trajectories received no alarm throughout execution out of 10,030 trajectories overall. This represents 7.85% of failures, indicating a relatively low overall missed-alarm proportion.

Thank you again for your time and thoughtful feedback. With two days remaining in the discussion period, please let us know if any questions or concerns remain after our responses. We would be happy to provide further clarification.

Reviewer_5G5NOpenReview ↗
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Paper summary

This paper proposes RESETTLE, a failure recovery framework for general frozen robot policies consisting of three modules: (1) a detector that triggers interventions when independently sampled action proposals exhibit disagreement; (2) a retrieval module that selects an observation of training demonstration as reference using an adapted V-JEPA representation; and (3) a residual policy that combines a reference-directed state-servo prior with a learned visual residual. Each intervention executes one corrective action before hand-over control to the original policy.

The framework is evaluated across four simulation settings and four real-world manipulation tasks using several VLA and WAM policies. The authors report consistent improvements in macro-average task performance, alongside lower reported monitoring-and-recovery computation latency than VLM-based (or agent-based) recovery approaches.

Critical strengths

1. Important and timely problem.

Enabling autonomous recovery without human intervention or expensive VLM reasoning is an important challenge for reliable, long-horizon robotic operation. The paper directly solves such problem.

2. Practical and modular framework.

The approach can augment different frozen generative policies through a shared recovery module within each embodiment. Its modularity: intervention detector, reference retrieval policy, and retrieval policy is appealing, as each component can be individually improved.

3. Broad empirical evaluation.

The experiments span several simulation benchmarks, different VLA and world-action policy architectures, and real-world manipulation tasks. The positive results across these settings suggest that the overall system has practical value.

Critical weaknesses

1. Recovery policy

My primary concern is whether the learned residual policy can actually generalize to the failure states for which it is intended.

The recovery controller is trained exclusively using successful demonstrations using HER style relabeling. During training, the current observation is paired with a future reference from the same trajectory, and the residual is supervised to reproduce the expert's nominal action after subtracting the state-servo prior (Appendix B.4, Eq. 13).

At deployment, however, the controller must generate corrections from potentially off-demonstration states toward references retrieved from different trajectories. Hence whether such inference-time residuals is in distribution of the residuals resulted from HER-style relabeling is unclear. Also, the residual policy is conditioned on the failure observation (Eq. 10) which is out-of-distribution. The detailed analysis on why we should expect a reliable prediction from residual policy would validate the design choice of residual policy.

This concern is especially important given the ablation in Table 1. Adding the learned visual residual to the state-servo-only controller improves aggregate success by only 2.1, 0.8, and 1.5 percentage points for FastWAM, Pi0.5, and QwenPI, respectively. The larger gains under robot-initialization perturbations indicate that the residual can be useful, but its contribution to recovery from genuine execution failures remains unclear.

2. Intervention detector

The detector measures disagreement between two action chunks sampled independently under identical conditioning. However, disagreement can arise from legitimate multimodality in a generative policy, rather than uncertainty about the correct behavior or impending task failure. Conversely, a policy can confidently and consistently generate incorrect actions, resulting in low disagreement.

This issue relates closely to the motivation for STAC (Agia et al., Unpacking Failure Modes of Generative Policies: Runtime Monitoring of Consistency and Progress, CoRL 2024). STAC instead measures the temporal consistency of predicted action distributions, specifically to account for multimodal generative behavior. Although the present paper cites Agia et al., the methodological distinction and its implications deserve more explicit discussion.

The authors do provide useful evidence: Appendix Table 9 compares action disagreement with V-JEPA feature distance as failure-detection signals, and Table 12 evaluates several disagreement thresholds. However, these experiments do not establish whether disagreement is preferable to alternative detectors when integrated into the same end-to-end recovery system.

Requested evidence Compare against STAC and simpler alternative action-based detectors while keeping retrieval and recovery fixed. Report detection accuracy, unnecessary interventions, detection delay, computational overhead, and final task success, ideally at matched intervention rates or computational budgets. A controlled multimodal task would be particularly informative.

3. Retrieval Policy

The retrieval module selects the nearest same-task demonstration frame in the adapted V-JEPA feature space. While the motivation for using action-aware visual representations is plausible, the paper does not directly establish that this representation produces more useful recovery references than simpler alternatives.

In particular, visual similarity does not necessarily imply that the associated robot state is reachable, appropriate for the current contact configuration, or useful for recovering task progress. I believe execution-aligned V-JEPA could be more aware of such property, however an empirical evidence would be required to support this claim.

Requested evidence: Compare adapted V-JEPA against frozen V-JEPA, another standard pretrained visual encoder, and a robot-state-based retrieval baseline. Keeping the detector and servo-only controller fixed would provide a particularly clean measurement of retrieval quality. An ablation removing the auxiliary dynamics-prediction objective would further clarify whether execution-aligned JEPA training contributes to the final system.

Questions for authors

Recovery scheduling: why exactly one corrective action?

The paper specifies that each intervention executes one native corrective action, resets the disagreement history, and returns control to the frozen base policy. This is a reasonable design for minimizing intervention duration, but it is not clear whether it is appropriate across different failure types.

For example, Appendix Table 11 reports an average of 25.32 takeovers per trajectory under robot-initialization perturbations. Repeated single-step corrections might be less effective than a short, sustained recovery sequence with re-observation and an explicit termination criterion.

Have you compared the current one-step strategy against short fixed-duration and adaptive-duration recovery, under comparable recovery-action budgets? Since computational efficiency is central to the paper, it would also be useful to distinguish the latency of producing one corrective action from the total time and number of interventions required to resolve a failure.

4 comments

Thank you for recognizing the importance of autonomous recovery, the modularity of our framework, and the breadth of our evaluation. Your comments identify important questions about residual generalization, detector selection, retrieval quality, and recovery duration. We address these below with additional experiments and clarify what the results establish.

1. Generalization of the learned residual

Our recovery module is initialized from V-JEPA2-AC, which underwent action-conditioned pretraining on DROID. Its visual and action-related representations learned from real-world robot interactions provide a foundation for transfer across scenes. Building on these representations, we combine an explicit state-servo prior with a residual adjustment conditioned on both current and reference observations to accommodate the execution state.

Our additional three-run QwenPI evaluation on LIBERO Plus provides evidence of a repeatable aggregate benefit: mean success increases from 83.2% with servo-only recovery to 84.6% with the visual residual, an improvement of 1.4 percentage points. Under Robot Initial States perturbations, the mean improvement is 6.0 percentage points. These results support the effectiveness of pretrained representations combined with residual adaptation under the evaluated perturbations.

2. Detector comparisons with retrieval and recovery fixed

Our detector compares two samples under identical current conditioning, whereas STAC measures temporal consistency between predicted action distributions.

We added comparisons on LIBERO Plus with QwenPI, keeping retrieval and recovery fixed. H denotes the predicted action-chunk length, and K denotes the number of actions executed before re-observation and replanning during nominal execution.

DetectorH8/K4 Success (%)Mean Recoveries/TrajectoryH16/K8 Success (%)Mean Recoveries/Trajectory
Our action disagreement, P95, two consecutive exceedances76.63.96778.92.557
STAC temporal distribution consistency75.53.96278.42.005
Temporal action L276.24.06778.22.068
Action magnitude49.333.54955.527.221
Random triggering75.13.96477.52.554
No recovery73.8075.80

Under H8/K4, our detector exceeds STAC and random triggering by 1.1 and 1.5 percentage points, respectively, at nearly identical intervention frequencies. It also exceeds temporal action L2 with slightly fewer recovery calls. Under H16/K8, our detector achieves the highest observed success.

We also examined 10,030 QwenPI trajectories, including 1,859 failures. Among these failures, 146 received no alarm throughout execution: 7.85% of failed trajectories and 1.46% of all trajectories. This indicates a relatively low overall proportion of failures without alarms.

3. Retrieval representations with the detector and servo controller fixed

We compared adapted V-JEPA, frozen V-JEPA, DINOv3, robot-state-based and random-reference retrieval on LIBERO Plus with QwenPI, keeping the detector and servo-only controller fixed. The base policy and full method are included for context.

All entries are success rates (%); All-task Average is weighted by task counts.

VariantQwenPI / BaseRandom Reference + ServoAdapted V-JEPA + ServoFrozen V-JEPA + ServoDINOv3 + ServoRobot State + ServoAdapted V-JEPA + Servo + Residual
Background97.698.098.698.398.398.598.6
Camera55.757.957.956.956.757.059.9
Language94.594.994.794.894.794.694.7
Light98.098.297.897.797.697.697.8
Layout79.179.779.679.979.479.580.1
Robot61.063.776.467.975.873.382.4
Noise86.287.386.686.586.686.686.9
All-task Average80.281.483.181.782.882.584.6

With the detector and servo controller fixed, adapted V-JEPA achieves the highest overall success among the retrieval alternatives, exceeding frozen V-JEPA, DINOv3, and robot-state retrieval by 1.4, 0.3, and 0.6 percentage points, respectively. This provides downstream evidence that adaptation improves the usefulness of retrieved references overall.

4. One-step versus sustained recovery

We evaluated one-step, fixed two-step, fixed four-step, and adaptive one-to-four-step recovery on LIBERO Plus with QwenPI.

VariantQwenPI / BaseOne-stepFixed 2-stepFixed 4-stepAdaptive 1–4-step
Background97.698.698.798.698.6
Camera55.759.960.260.060.0
Language94.594.794.594.894.8
Light98.097.897.897.797.6
Layout79.180.179.779.980.0
Robot61.082.480.282.081.9
Noise86.286.987.286.986.9
All-task Average80.284.684.284.584.5

Success rates are percentages. We additionally measured intervention segments and cumulative corrective actions, averaged over all trajectories:

MetricOne-stepFixed 2-stepFixed 4-stepAdaptive 1–4-step
Mean intervention segments per trajectory3.112.321.711.73
Mean corrective actions per trajectory3.114.646.846.78

Longer recovery reduces intervention segments but increases cumulative corrective actions without improving aggregate success in this evaluation. For example, fixed four-step recovery reduces segments from 3.11 to 1.71, while increasing corrective actions from 3.11 to 6.84—approximately 2.2 times as many. Under Robot perturbations, one-step recovery also retains the highest observed success among these schedules. These results support one-step recovery as an economical default that returns control promptly to the base policy.

Thank you for the additional experiments and detailed responses. I appreciate the new controlled comparisons. However, my primary concerns regarding W1 and W2 remain only partially addressed.

W1 — Recovery policy generalization. My main concern is whether and why should the residual policy can reliably generalize. Residual policy is learned from nominal demonstration transitions and deployed to off-demonstration recovery states. Without an inductive bias or generalization/extrapolation mechanism, I see little to no justification on why residual policy should generalize. Furthermore, the empirical improvement gain is within the scale of noise.

W2 — Intervention detector. I appreciate the controlled comparison against STAC and other detectors. However, my concern is whether disagreement is a reliable indicator of execution failure, rather than legitimate action multimodality.

Overall, while the additional experiments strengthen the empirical evaluation, I remain concerned that the reliability of the proposed recovery mechanism and intervention detector has not been sufficiently established.

With these concerns un-addressed, I would like to keep my score unchanged.

Thank you for carefully considering our additional experiments and for clarifying your remaining concerns about the generalization of the residual policy and the reliability of the intervention detector. We appreciate the opportunity to address these points more directly and provide further supporting evidence below.

W1 — Recovery policy generalization

The residual is trained to predict the difference between the demonstrated action and the reference-derived servo action. Successful demonstrations therefore provide supervision for scene-dependent adjustments to direct state alignment. Our design combines an explicit geometric prior with a visually conditioned correction, constrained in direction and magnitude and executed for one step before re-observation. This provides an inductive bias for transferring local adjustments to execution deviations with similar manipulation structure.

Visual adjustment is particularly relevant in two contact-rich situations: (1) the arm or gripper is obstructed by surrounding objects, and (2) the robot has an unfavorable grasp pose. In these situations, directly servoing toward the reference robot state can cause collisions or inappropriate motions because it ignores the current object configuration. The visual residual uses current and reference observations to adjust this motion, helping avoid such behavior. Figures 4–5 and the supplementary videos illustrate these recovery scenarios with the full system.

The controlled ablation isolates the residual’s contribution. Across three QwenPI evaluations on LIBERO Plus, success increases from 83.16% ± 0.02% to 84.56% ± 0.01% (mean ± sample standard deviation). Individual gains are 1.36, 1.42, and 1.42 percentage points, with a mean gain of 6.04 points under Robot Initial States perturbations. These improvements exceed the observed run-to-run variation and support repeatable benefits under the evaluated perturbations.

W2 — Action disagreement and legitimate multimodality

Regarding W2, we focus on the practical value of action disagreement for selecting when to intervene. To further assess this, we randomly sampled 200 episodes identified as having high action disagreement from both ultimately successful and failed trajectories. Visual inspection found unreasonable actions in 184 episodes (92%), while actions appeared reasonable in only 16 (8%). Our supplementary videos also compare the triggering moments, execution behavior without correction, and the corrective behavior of our method, providing qualitative support for the appropriateness of intervention timing.

Table 9 shows a clear difference in both trigger rates and trigger counts: 77.89%–100% of failed trajectories trigger the detector, compared with 9.22%–42.81% of successful trajectories. Among trajectories with at least one trigger, failed trajectories average 9.6–27.4 triggers, versus only 1.3–4.9 for successful trajectories. Thus, high disagreement occurs more repeatedly in failed trajectories. Additionally, among 10,030 inspected QwenPI trajectories, 1,859 failed, and only 146 received no alarm throughout execution—7.85% of failed trajectories.

More direct evidence comes from the controlled comparison with retrieval and recovery fixed. Under H8/K4—predicting eight actions and executing four before re-observation and replanning during nominal execution—our trigger and random triggering have nearly identical recovery frequencies (3.967 versus 3.964 per trajectory, averaged over all trajectories), but achieve success rates of 76.6% and 75.1%, respectively. This supports the value of disagreement-based intervention timing beyond intervening randomly at a similar frequency.

Related work VLA-ATTC [1] likewise uses the DTW distance between two action chunks sampled under identical conditioning to decide when to allocate additional computation and select candidates using a critic. Its experiments show strong agreement between this indicator and human judgments of scene difficulty. We acknowledge that legitimate multimodality can also produce disagreement; our evidence supports disagreement as a useful intervention signal, rather than implying that every disagreement necessarily indicates task failure.

[1] Li et al.VLA-ATTC: Adaptive Test-Time Compute for VLA Models with Relative Action Critic Model. ICML, 2026.

Reviewer_jqf5OpenReview ↗
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Paper summary

The paper introduces RESETTLE, an action-level recovery framework for frozen generative robot policies. It detects potential execution difficulties when two independently sampled action proposals exceed a calibrated disagreement threshold at two consecutive policy decisions under identical conditioning. Once triggered, an adapted V-JEPA encoder retrieves a reference demonstration from the same task. A state-servo prior, refined by a guarded visual residual, generates a single corrective action before control returns to the base policy. The recovery module is trained offline and requires neither online trajectory optimization nor additional VLM reasoning for recovery at deployment. Experiments with six base policies on LIBERO-Plus, Meta-World, and RoboCasa Tabletop show improvements in aggregate success rates. RESETTLE is also evaluated on LIBERO-Pro Swap and four real-world manipulation tasks. Ablation studies assess the contribution of the visual residual, while latency comparisons measure the computational costs of monitoring and recovery.

Critical strengths

Broad evaluation across policies and tasks. The evaluation covers six base policies, three main simulation benchmarks, multiple robot action interfaces, and four real-world manipulation tasks, including 10,030 LIBERO-Plus evaluation cases. The recovery modules are shared across base policies within each setting, and paired comparisons keep the base-policy weights fixed. The aggregate success-rate improvements across these settings provide evidence of RESETTLE’s applicability across different frozen policies, rather than dependence on a single backbone.

Ablations show the benefit of visual refinement. Table 1 compares state-servo-only recovery with the full method across three policies. Adding the guarded visual residual improves aggregate success rates by 2.1, 0.8, and 1.5 percentage points for FastWAM, π0.5, and QwenPI, respectively. The gains are modest but consistent across all three policies, suggesting that visual refinement provides additional benefits beyond reference-state tracking alone.

Critical weaknesses

The current experiments do not distinguish the effect of the recovery controller from that of increased feedback frequency. During an intervention, the pending base-policy actions are replaced by a corrective action, and only one native control tick is executed before a fresh observation and replanning. The resulting gains may therefore partly reflect a shorter execution horizon and more frequent feedback, rather than the reference-guided correction itself. The servo-only ablation does not address this issue, as it uses the same intervention protocol. A useful control would apply the same trigger rule but execute only the first base-policy action before re-observing and replanning, without invoking the recovery controller. Without this comparison, the contribution of the recovery mechanism to the observed gains remains difficult to assess.

Comparisons with alternative recovery methods do not establish the overall effectiveness–cost tradeoff. Table 6 reports computational latency for Agentic Robot, VoLoAgent, and adapted LPB, but does not compare task success under a common evaluation protocol. The methods also produce different outputs: RESETTLE generates a single corrective action, whereas VoLoAgent produces a trajectory. Their per-invocation latencies therefore do not directly reflect their relative recovery efficiency. The reported measurements still provide useful information about computational cost, and the paper acknowledges their limitations. However, lower latency alone does not establish a better overall effectiveness–cost tradeoff. Without corresponding task-success comparisons, the evidence is insufficient to establish RESETTLE's overall advantage over existing recovery methods.

Questions for authors

1. Controlled Comparison of Execution Mechanisms

Under the same trigger rule, counter-reset protocol, and environment-step budget, how does RESETTLE perform relative to a control that uses the same trigger but executes only the first base-policy action before re-observing and replanning, without invoking the recovery controller? If this control has not been evaluated, do the existing experiments or logs offer any evidence that reference-guided correction contributes to the gains beyond the effects of shorter execution horizons and more frequent feedback?

2. Recovery Effectiveness and Computational Cost

For the recovery methods in Table 6, can the authors report task-success results on matched tasks under comparable execution budgets, along with cumulative computation time or task-completion time where available? RESETTLE generates a single corrective action, whereas VoLoAgent prepares a trajectory. How should their per-invocation latencies be interpreted given this difference? Even a comparison on a shared subset of tasks would help establish whether RESETTLE's lower computational cost comes with comparable recovery effectiveness.

3. Statistical Reliability of the Reported Improvements

Some of the reported gains, particularly those from adding the visual residual, are relatively small. Could the authors provide uncertainty estimates, results from repeated seeds, or paired success/failure counts for the main comparisons, especially the servo-only ablation? If repeated evaluations are unavailable, a discussion of how evaluation variability might affect the reported gains would still be useful. This would help clarify how confidently the improvements can be attributed to the proposed design choices.

4. Reconciling Trigger Statistics with Actual Takeovers

Under Noise perturbations, Table 9 reports action-disagreement triggers in 99.05% of failed trajectories and 42.81% of successful trajectories, while Table 11 reports actual recovery takeovers in 8.00% of trajectories. How are detected triggers translated into executed takeovers, and how often are interventions skipped because no same-task reference is available? It would also be helpful to clarify whether earlier interventions change subsequent execution trajectories and affect the reported statistics.

4 comments

Thank you for recognizing our evaluation across policies and tasks and the additional benefit of visual refinement. We address your concerns with the following experiments and corrected statistics.

1. Separating corrective control from increased feedback frequency

We added the suggested control on LIBERO Plus with QwenPI, keeping the triggering rule, counter-reset protocol, and environment-step budget identical. At each trigger, the control executes only the first base-policy action before re-observing and replanning, without invoking recovery.

The table reports success rates (%); the overall average is weighted by task counts.

MethodBackgroundCameraLanguageLightLayoutRobotNoiseOverall
QwenPI / Base97.655.794.598.079.161.086.280.2
First-action-only replanning98.355.494.798.179.356.586.379.6
QwenPI / RESETTLE98.659.994.797.880.182.486.984.6

Shortening execution alone does not improve aggregate success, whereas RESETTLE exceeds this control by 5.0 percentage points. This supports the contribution of reference-guided correction beyond earlier re-observation and replanning.

2. Recovery effectiveness and cumulative computation

We reproduced VoLoAgent and VLA-Corrector on the full LIBERO Plus benchmark using QwenPI as the underlying policy. The comparison covers all tasks across all seven perturbation variants.

MethodSuccess RateMean Cumulative Online Computation Time per Trajectory
No recovery80.2%3.12 s
VLA-Corrector81.4%10.76 s
VoLoAgent68.5%7.16 s
RESETTLE84.6%2.48 s

RESETTLE achieves the highest success rate and lowest cumulative online computation in this evaluation. It improves success over no recovery by 4.4 percentage points and exceeds VLA-Corrector and VoLoAgent by 3.2 and 16.1 points, respectively. VLA-Corrector and VoLoAgent require approximately 4.34 and 2.89 times as much online computation as RESETTLE. Mismatches between decomposed subtask instructions and QwenPI’s behavior, together with delayed subgoal transitions, explain VoLoAgent’s lower success in this evaluation.

3. Statistical reliability of the residual gains

We conducted three repeated evaluations of the servo-only and residual-augmented variants:

MethodMean Success Rate ± Sample Standard Deviation
State-servo only83.16% ± 0.02%
State-servo + visual residual84.56% ± 0.01%

The improvements were 1.36, 1.42, and 1.42 percentage points, averaging 1.40 points and exceeding the observed run-to-run variation. Mean gains under Robot and Camera were 6.0 and 2.0 percentage points, respectively. This supports repeatability within the evaluated setting.

4. Correcting trigger and takeover statistics

Thank you for identifying the issue in the original Table 11. We recomputed the statistics from actual execution trajectories with recovery enabled:

PerturbationTrajectories with Takeover / TotalTakeover RateTotal Recovery ActionsMean Recovery Actions/Trajectory
Background114 / 1,07610.59%3470.322
Camera910 / 1,59956.91%9,6776.052
Language194 / 1,53712.62%6030.392
Light152 / 1,14213.31%4020.352
Layout425 / 1,52527.87%3,9802.610
Robot822 / 1,55053.03%7,8425.059
Noise790 / 1,60149.34%8,2895.177
All tasks3,407 / 10,03033.97%31,1403.105

The corrected Noise takeover rate is 49.34%, replacing 8.00%; we apologize for this reporting error. Table 9 reports trigger rates separately within failed and successful trajectories, whereas Table 11 reports actual takeovers across all trajectories. Earlier recovery actions also change subsequent observations, actions, and trigger opportunities.

Thank you again for your time and thoughtful feedback. With two days remaining in the discussion period, please let us know if any questions or concerns remain after our responses. We would be happy to provide further clarification.

Reviewer_jqf5OpenReview ↗

Follow-up on the Authors’ Response

Thank you for the additional controlled experiments. The new results address several of my concerns:

  • The first-action-only replanning control supports a benefit from reference-guided correction beyond increased feedback frequency. The added task-success and cumulative computation results also provide a stronger basis for comparing recovery effectiveness and cost.
  • The three repeated evaluations support the repeatability of the visual residual’s gains. The corrected takeover statistics, together with the clarification that no interventions were skipped because of missing references, also address my question about trigger and takeover rates.

I would still like the following points clarified:

  1. Please specify whether cumulative computation includes base-policy inference, sampling both action proposals, and all monitoring and recovery calls. The environment-step budgets and monitoring frequencies for each method should also be stated so that the comparison can be assessed.
  2. Please clarify which trajectory sets, checkpoints, evaluation seeds, and recovery settings were used for Tables 9, 11, and 23. For example, the Language counts in Table 23 imply a trigger rate of 65.33% among failed trajectories, whereas Table 9 reports 77.89%. If these results come from different runs or settings, please explain the difference. The additional experiments have substantially reduced my concerns.

Thank you for the suggestion. Cumulative computation includes base-policy inference, action-proposal sampling, observation processing, all monitoring and recovery calls, and communication throughout each trajectory; it excludes model loading, environment simulation, video encoding, and warm-up. Sampling both proposals is included in the shared-task timing comparison. RESETTLE monitors at each fresh policy decision, normally every eight environment steps, and requests a new observation and plan immediately after one-step recovery. VoLoAgent uses a configured 40-step monitoring interval, while VLA-Corrector monitors every step. All methods share the same environment-step limits, including recovery actions.

We apologize for the insufficient explanation of the statistical populations. Table 9 measures offline alarms on no-recovery trajectories, whereas Table 23 uses the online recovery trajectories of corrected Table 11, grouped by their final outcomes after recovery. For Language, these yield 74/95 = 77.89% and (75−26)/75 = 65.33%, respectively. Although the checkpoint, P95 threshold, and two-consecutive-exceedance rule are identical, recovery changes subsequent trajectories and outcomes. Table 23 therefore reports the no-alarm fraction among ultimately failed trajectories, rather than an event-level false-negative rate.

Reviewer_DyT1OpenReview ↗
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Paper summary

The paper proposes RESETTLE, a model-agnostic recovery framework that acts on the frozen robot policy execution interface. The system triggers recovery through the continuous divergence of two independent action samplings under the same conditions. It uses the adapted V-JEPA encoder to retrieve the reference state from the same task demonstration library, then combines the state-servo prior with the constrained visual residuals to perform a corrective action, and then returns control to the base policy. The experiments cover six basic policies, LIBERO-Plus, Meta-World, RoboCasa Tabletop, LIBERO-Pro Swap, and four real robot tasks, and report lower additional computational latency compared to VLM inference or online planning schemes.

Critical strengths
  1. Integrate abnormal monitoring, demonstration retrieval, and local correction into a clear execution-level recovery process, without the need for fine-tuning of the basic strategy or online trajectory optimization.
  2. The evaluation scope is wide, covering WAM, VLA, diffusion or autoregressive strategies, multiple simulation benchmarks, real robot tasks, and high-level agentic planners, fully demonstrating the compatibility of the interface layer method.
  3. The action divergence trigger does not require task failure labels, and the threshold is only calibrated based on the inference distribution of the training data, with a relatively low deployment threshold.
  4. The computational efficiency analysis is relatively complete. Under the unified QwenPI configuration, the monitoring and recovery costs of RESETTLE are significantly lower than those of Agentic Robot, VoLoAgent, and the adapted LPB.
Critical weaknesses
  • The reliance on a task-specific success demonstration library for retrieval limits the scalability of the open scenarios.
  • The retrieval only uses cosine nearest neighbors. If the retrieved frames are out of sequence or do not match the reference frames of the current execution stage, it will introduce incorrect servo priors. Has the paper conducted a statistical analysis of cases where the retrieval failed?
  • How significant is the influence of the size of the reference bank (a few demos / full demos) on the final success rate?
  • It is suggested to add comparison with the other methods of inference-time recovery.
  • When the policy consistently takes the same but incorrect actions, recovery will not be triggered. The paper lists such cases, but lacks statistics on the frequency of missed detection.
Questions for authors

Please refer to Weakness

1 comment

Thank you for recognizing the modularity, broad applicability, and computational advantages of RESETTLE. We address your concerns with additional experiments on LIBERO Plus using QwenPI.

1. Dependence on same-task demonstrations

We evaluated cross-task retrieval using a shared reference library under two settings: Include contains demonstrations from all eight evaluated tasks, while Exclude removes all demonstrations of the current target task and permits retrieval only from the other seven tasks.

We evaluated all 2,003 official perturbed instances of these tasks, once per instance using seed 7.

SettingSuccessful InstancesOverall Success (%)
No recovery1,65382.5
Include target-task demonstrations1,67683.7
Exclude target-task demonstrations1,67583.6

All 3,364 corrective actions in Exclude used cross-task references. Removing target-task demonstrations resulted in only one fewer successful instance than Include, while retaining an improvement over the baseline. This suggests that recovery can benefit from other tasks’ demonstrations.

2. Statistical analysis of retrieval mismatches

We visually inspected 240 actual interventions from 211 trajectories, covering 28 suite × variant combinations.

CategoryAssessment CriterionCountStratified Weighted Proportion
Phase-compatibleCompatible manipulation phases18275.83%
Phase mismatchIncompatible manipulation phases3715.4%
Interaction-object mismatchDifferent target objects31.25%
Geometric mismatch riskBroadly matching phase and object, but potentially unsuitable position, orientation, or spatial relationships187.5%

Phase mismatches do occur, but most retrieved references are compatible with the current execution phase. This suggests that adapted V-JEPA2-AC provides some phase-discriminative information for retrieval.

3. Effect of reference-library size

We varied the number of reference demonstrations per task. Success rates (%) are shown below; All-task Average is weighted by the actual task counts.

References per TaskBackgroundCameraLanguageLightLayoutRobotNoiseAll-task Average
QwenPI / Base97.655.794.598.079.161.086.280.2
198.356.494.998.179.663.286.680.9
298.557.294.698.179.469.286.481.9
498.157.794.797.779.377.786.683.2
898.559.994.697.779.779.086.683.9
2098.259.095.097.979.579.286.783.8
3298.260.094.998.079.979.586.584.0
All (approximately 42)98.659.994.797.880.182.486.984.6

Larger libraries generally improve success, with diminishing and not strictly monotonic gains. Eight demonstrations per task achieve 83.9%, close to the full library’s 84.6%, compared with 80.2% for the base policy.

4. Comparison with another inference-time recovery method

We reproduced VoLoAgent and VLA-Corrector on the full LIBERO Plus benchmark using QwenPI as the underlying policy. The comparison covers all tasks across all seven perturbation variants.

MethodSuccess RateMean Cumulative Online Computation Time per Trajectory
No recovery80.2%3.12 s
VLA-Corrector81.4%10.76 s
VoLoAgent68.5%7.16 s
RESETTLE84.6%2.48 s

RESETTLE achieves the highest success rate and lowest cumulative online computation in this evaluation. It improves success over no recovery by 4.4 percentage points and exceeds VLA-Corrector and VoLoAgent by 3.2 and 16.1 points, respectively. VLA-Corrector and VoLoAgent require approximately 4.34 and 2.89 times as much online computation as RESETTLE. Mismatches between decomposed subtask instructions and QwenPI’s behavior, together with delayed subgoal transitions, may explain VoLoAgent’s lower success in this evaluation.

5. Frequency of failures without alarms

We analyzed 10,030 QwenPI trajectories, including 1,859 failures. Of these failures, 146 received no alarm throughout execution, accounting for 7.85% of failed trajectories and 1.46% of all trajectories.

Among these 146 trajectories, 27 never exceeded the threshold, while 119 exceeded it at least once but did not satisfy the two-consecutive-exceedance requirement. Thus, most failures without alarms involved threshold exceedances that did not meet the temporal confirmation criterion. Overall, the proportion of failed trajectories receiving no alarm was relatively low at 7.85%.

Comments on the paper

1 comment

Dear Reviewers,

We sincerely thank all reviewers for their careful reading and constructive suggestions, which have helped improve the clarity and completeness of our work.

We have revised the manuscript to address the concerns and questions raised above. All changes are highlighted in blue in the revised PDF.

Best regards, Authors of Paper 2949

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

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