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Under review as a conference paper at ICLR 2027

Policy-Aligned Predictive Verification for Adaptive VLA Action-Chunk Execution

Abstract

Vision-language-action (VLA) policies generate action sequences that reduce repeated inference, but deciding how much of each sequence to execute is critical to task success. Existing adaptive methods make this decision using generation stability or prediction agreement, yet these signals do not establish whether executing a candidate prefix preserves the ability to complete the task. We introduce a *policy-aligned predictive verifier* (PAV) that anticipates the consequences of candidate action prefixes and evaluates their compatibility with successful continuation before execution. Rather than using future prediction to generate actions, our method evaluates existing proposals in the VLA's internal task-conditioned representation space. To learn local judgments from terminal task outcomes, we combine trajectory-level survival supervision with a localization prior that preserves useful behavior within failed rollouts. The resulting validity scores guide execution-horizon selection. Evaluations with and across LIBERO, RoboTwin 2.0, and real-world manipulation show improved success–query trade-offs. These findings point toward a different role for future prediction in robotics, using it to assess how far to trust a policy's proposed actions rather than to generate new ones.

Primary area:
applications to robotics, autonomy, planning
Keywords:
Vision-Language-Action Models, Adaptive Action-Chunk Execution, Predictive Verification, Policy-Aligned Future Prediction, Trajectory-Level Supervision

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Paper summary

The paper proposes a policy-aligned predictive verifier (PAV) that predicts the consequences of candidate action prefixes in a VLA policy’s internal representation space and estimates their compatibility with successful task continuation. These estimates determine how many actions to execute before obtaining a new observation and replanning. The verifier is trained using trajectory-level success/failure supervision, with a localization prior intended to preserve valid behavior within failed rollouts. Evaluations with Pi0 and Pi0.5 on LIBERO, RoboTwin 2.0, and real-world manipulation tasks show improved trade-offs between task success and policy-query cost.

Critical strengths
  1. The paper asks whether executing a proposed prefix preserves successful continuation, rather than relying solely on action-generation stability or prediction agreement. This directly connects horizon selection to the task objective.
  2. Learning local judgments from coarse supervision. The trajectory-level objective and localization prior provide a way to train the verifier from terminal outcomes without requiring action-level validity annotations.
  3. Experiments span two VLA policies, simulation benchmarks, and real-world tasks. Ablations examine future prediction, policy representations, loss terms, and score normalization. The reported additional GPU computation is small.
Critical weaknesses
  1. The improvement over the strongest adaptive baseline is modest. PAV achieves slightly higher success than AutoHorizon in the reported LIBERO H=50 settings but requires more policy queries. The advantage at comparable query budgets remains unclear.
  2. Performance shows a sharp peak at the default acceptance threshold, raising concerns about robustness to this hyperparameter.
  3. Several real-world implementation and evaluation details remain unspecified, limiting reproducibility.
Questions for authors
  1. How was beta=0.90 selected for the threshold, and was this choice made exclusively using validation data? how robust is its performance across repeated runs given the sharp peak at beta=0.90?
  2. Have you directly tested whether low-scoring action extensions reduce subsequent task success, or is the verifier validated only through overall execution performance?
  3. Does inference and verification block robot execution or overlap with ongoing motion? Please clarify the real-world details marked “TBD” and report end-to-end latency if available.
7 comments

[W2,Q1] Threshold Selection and Sensitivity

We apologize for not clearly explaining the selection of β=0.90\beta=0.90 and the sensitivity to this threshold. We selected the threshold using only validation data separate from the final evaluation data. Specifically, for each sample, we used the minimum of its first two prefix scores as its representative score. Because the first horizon extension is a shared prerequisite for all subsequent extensions, this choice aims to calibrate the criterion for extending execution beyond the minimum length. We then applied Kittler’s method, which approximates the score distribution with two Gaussians and minimizes the separation error. The resulting thresholds were 0.906771 for LIBERO–π0\pi_0–H50, 0.900278 for LIBERO–π0.5\pi_{0.5}–H10, 0.898986 for LIBERO–π0.5\pi_{0.5}–H50, and 0.907220 for RoboTwin–π0.5\pi_{0.5}–H32. To evaluate transferability across tasks and environments, we applied a common threshold of β=0.90\beta=0.90 in all experiments. These results support the applicability of a shared threshold in the evaluated environments, but do not establish its optimality in every environment. Also, to address your question about robustness across repeated runs, we evaluated PAV at β=0.90\beta=0.90 across three evaluation seeds. Its mean success rate was 94.88% (±\pm 0.45%). This provides evidence of stable performance at the default threshold across these runs.

We additionally compared the unrounded shared, suite-specific, and task-specific thresholds on LIBERO–π0.5\pi_{0.5}–H50, as shown below. The suite-specific thresholds were 0.9123 for Spatial, 0.8961 for Object, 0.9147 for Goal, and 0.8892 for Long. Nevertheless, we acknowledge that threshold sensitivity is a limitation of our method.

\begin{array}{lrrrrrr} \text{Threshold setting} & \text{Spatial} & \text{Object} & \text{Goal} & \text{Long} & \text{Overall success rate} & \text{Average queries} \\ \hline \text{Shared Kittler }(\approx 0.899) & 97.0\% & 98.6\% & 91.8\% & 91.2\% & 94.65\% & 13.74 \\ \text{Suite-specific Kittler} & 96.8\% & 99.0\% & 91.4\% & 92.2\% & 94.85\% & 11.92 \\ \text{Task-specific Kittler} & 96.4\% & 98.4\% & 94.6\% & 93.0\% & 95.60\% & 12.38 \end{array}

The substantial performance variation around β=0.90\beta=0.90 can be understood through the trade-off between the temporal consistency of longer execution and the responsiveness of shorter execution. A lower threshold permits longer execution, but may delay necessary reactions, allowing errors to accumulate and leading to states from which success is difficult. We also observed more frequent short executions following long executions, consistent with attempts to recover from accumulated errors. Specifically, lowering β\beta from 0.90 to 0.88 increased the proportion of h≥20h \geq 20 selections from 21.88% to 42.92% and that of h=5h=5 selections from 24.99% to 36.59%, while reducing the success rate from 94.65% to 82.75%. Furthermore, the number of episodes in which a long execution (h≥20h \geq 20) was followed by low scores for h=5h=5 for at least three consecutive observation steps increased from 59 at the reference threshold (β≈0.899\beta \approx 0.899) to 97 at β=0.88\beta=0.88. This is consistent with repeated short executions in states assessed as having a low likelihood of success after a long execution. It suggests that even frequent h=5h=5 selection may not prevent performance degradation if the system fails to respond when needed.

Conversely, a higher threshold imposes stricter conditions on execution extension. Although shorter execution provides responsiveness, it limits the benefits of temporal consistency and query reduction offered by longer execution. The method still selects some longer action chunks and outperforms fixed h=5h=5 execution, but appears unable to fully exploit these benefits. Specifically, at β=0.92\beta=0.92, the h=5h=5 selection rate was 53.12%, and the average number of queries increased from 14.0 at β=0.90\beta=0.90 to 25.1. The success rate decreased from 94.65% to 88.30%, although it remained above the 87.15% achieved with fixed h=5h=5 execution. These results are consistent with the trade-off discussed in the introduction. They highlight the importance of choosing a threshold that provides longer execution for consistency and shorter execution for responsiveness when each is needed.

[Q2] Direct Evaluation of Low-Scoring Action Extensions

Thank you for this helpful question. We directly evaluated whether executing low-scoring action extensions reduces subsequent task success rates, separately from overall execution performance. We focused on this analysis and conducted comparisons across candidates and execution lengths as supporting analyses.

We randomly sampled states within each suite from episodes used for neither training nor model selection. We then selected states based solely on variation in continuation success rates across candidates or prefix lengths. This selection did not use verifier scores or their agreement with continuation outcomes. This selection did not use verifier scores or their agreement with continuation outcomes. At each state, we computed scores for eight action candidates before execution. We then restored the same simulator state to execute each prefix and performed eight continuations per candidate–length pair using a common FixedH10 continuation policy. Repetition seeds, success criteria, and episode time limits were identical across comparison conditions. Thus, the evaluation targets were newly measured continuation success rates after each prefix, rather than terminal labels from existing trajectories.

Our primary analysis compared the local score of each additional five-action segment with the corresponding change in success rate. For the same starting state and candidate, we computed the difference between the success rates after executing prefixes of length HH and H+5H+5, given by Δp=psuccess(H+5)−psuccess(H)\Delta p = p_{\mathrm{success}}(H+5) - p_{\mathrm{success}}(H). Holding the starting state and extension interval fixed, we calculated the Spearman correlation between the segment’s local score and Δp\Delta p across eight candidates. Across 100 interval comparisons, the median correlation was 0.3853. This supports an association between lower local scores and less favorable changes in success rate.

For example, for an H15 →\to H20 extension in the Goal suite, a low-scoring candidate and the highest-scoring candidate both had a success rate of 4/8 before extension. After extension, the low-scoring candidate’s success rate decreased to 1/8, while the highest-scoring candidate’s remained at 4/8. The correlation across all eight candidates in this comparison was 0.9262. Similarly, for an H20 →\to H25 extension in the Object suite, a low-scoring candidate’s success rate decreased from 8/8 to 6/8, whereas the highest-scoring candidate’s increased from 3/8 to 6/8. The correlation across all eight candidates was 0.8225.

We also conducted two supporting analyses of cumulative prefix scores.

  • Comparing candidates at a fixed execution length, we held the starting state and prefix length fixed to assess whether the score distinguishes candidates with different continuation success rates. Across 100 comparisons, the Spearman correlation between prefix scores and continuation success rates had a mean of 0.3383 and a median of 0.2943.
  • Comparing execution lengths for a fixed candidate, we held the starting state and candidate fixed and compared H10, H20, and H30. Across 100 comparisons, the mean correlation was 0.7386, with a median of 0.8660.

These experiments provide direct validation beyond overall system performance. The supporting analyses show that prefix scores track subsequent success rates, while the extension analysis directly demonstrates an association between lower local scores and less favorable changes in success rate. Although evaluated using a FixedH10 continuation policy, these results provide evidence that the learned scores reflect meaningful variation in actual continuation success rates, including changes associated with executing additional action segments. We will clarify these findings and the supporting evidence in the paper.

[W1] Success–Query Trade-offs and Generalization Across Benchmarks

We agree that PAV sometimes requires more queries than AutoHorizon and that the difference in success rate can be modest. As discussed in our response to Q1, we used a fixed threshold across environments to demonstrate that a shared threshold can achieve strong performance. Using suite-specific or task-specific thresholds achieves slightly higher success rates with fewer queries than AutoHorizon. In the same LIBERO–π0.5\pi_{0.5}–H50 setting, AutoHorizon achieves a 94.45% success rate with 12.7 queries on average.

We also examined whether AutoHorizon’s reported RoboTwin performance extends to a shared policy checkpoint across tasks. The AutoHorizon paper reports results on seven RoboTwin tasks using checkpoints fine-tuned separately for each task. These results therefore do not directly establish its performance with a shared checkpoint trained across RoboTwin tasks. For a fair comparison, we evaluated AutoHorizon using the same checkpoint as PAV under matched evaluation conditions. The results are shown below.

\begin{array}{lrrr} \text{Method} & \text{Success rate}\uparrow & \text{Average queries}\downarrow & \text{Average execution horizon} \\ \hline \text{PAV} & 58.72\% & 56.75 & 10.25 \\ \text{AutoHorizon (reimplementation)} & 45.64\% & 14.53 & 29.77 \end{array}

In this setting, AutoHorizon predominantly selects the maximum horizon of 32, yielding an average execution horizon of 29.77. This suggests limited effective adaptation under the shared-checkpoint setting. Its success rate of 45.64% is also close to the 45.40% achieved by fixed H32 execution. In contrast, PAV uses a shorter average execution horizon of 10.25 and achieves a success rate 13.08 percentage points higher, while requiring more policy queries.

Together, these results support PAV’s effectiveness across multiple benchmarks. On LIBERO, suite-specific or task-specific thresholds improve success rates while reducing queries relative to AutoHorizon. On RoboTwin, PAV achieves a larger success-rate improvement at the cost of more queries.

[W3,Q3] Real-World Execution and Evaluation Protocol

Thank you for raising this important point. Our real-world system uses a sequential execution scheme without overlap between action execution and inference. After completing the action prefix selected at the previous decision, the system obtains a new observation, performs policy inference and verification, and then starts executing the next prefix. Execution of the next action therefore waits until inference and verification are complete. We apologize for not being able to report end-to-end latency, as we did not separately record this measurement.

We will also fill in the TBD entries in Appendix E.1–E.2. Success is judged by a human evaluator. For Tray, success requires releasing the cube from the gripper and placing it correctly inside the tray. For Stack, the cubes must remain stacked without collapsing after the gripper releases the cube. For Button, the button must be pressed and produce an audible click. The maximum execution budget is 500 action steps per trial, with no separate wall-clock time limit.

For each task, we use the checkpoint obtained after 10,000 updates of full fine-tuning of π0.5\pi_{0.5}, and train each verifier for 60 epochs on 50 rollouts. The candidate horizons are {5,10,…,50}\{5,10,\ldots,50\}, the shared threshold is β=0.90\beta=0.90, and square-root block-count normalization is applied. At each decision, we generate a single action chunk and execute the selected prefix without regenerating the chunk. Evaluation consists of 30 trials per task, separate from the training data, with initial object configurations matched across methods by episode index. Query counts include the initial generation, and the average horizon is computed by assigning equal weight to every selected prefix.

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Paper summary

This paper proposes Policy-Aligned Predictive Verification (PAV) for adaptive action-chunk execution in Vision-Language-Action (VLA) models. The method predicts future task-conditioned policy representations under candidate action prefixes and uses a learned verifier to estimate their compatibility with successful task continuation. The verifier is trained from trajectory-level success/failure labels with an additional localization regularizer, and the resulting scores determine the execution horizon.

Experiments on LIBERO, RoboTwin 2.0, and real-world manipulation tasks demonstrate improvements over fixed-horizon execution and competitive performance against existing adaptive execution methods. Ablations examine future prediction, representation choice, and the training objectives.

Critical strengths

S1. Meaningful problem formulation.

The paper addresses an important trade-off between execution efficiency and responsiveness in action-chunk-based VLA policies. Evaluating the consequences of proposed actions, rather than relying only on generation consistency, is a reasonable and interesting direction.

S2. Comprehensive empirical evaluation and ablations.

The experiments cover simulation and real-world manipulation. The comparisons with direct verification and DINOv2-based prediction, together with the loss-term ablations, provide useful evidence supporting the proposed design choices.

Critical weaknesses

W1. The learned verifier is not shown to estimate the proposed notion of continuation validity.

The central concept of the paper is proposal validity, defined in Eq. (4) as the probability that successful task continuation remains possible after executing a candidate prefix. However, the verifier is trained using only terminal trajectory outcomes (Eqs. (10)–(12)), without observing whether successful continuation is actually possible from intermediate states.

A failed trajectory may contain recoverable states, and its terminal failure does not necessarily imply that any particular preceding action prefix was invalid. Although the localization regularizer encourages low validity scores to concentrate on fewer extensions, it does not establish that these scores identify genuinely incompatible actions.

Furthermore, the length-normalized score used for horizon selection (Eq. (14)) is a heuristic rather than a calibrated continuation probability.

The paper provides no direct validation of the estimated proposal validity against actual continuation outcomes from candidate intermediate states. Consequently, the connection between the proposed theoretical formulation and the learned execution criterion remains insufficiently established.

W2. Limited improvement over strong adaptive baselines despite additional training and model complexity.

Although PAV substantially improves over several fixed-horizon baselines, its advantage over existing adaptive execution methods is considerably smaller.

For example, on LIBERO with π0.5 and H=50 (Table 1), PAV achieves 94.65% success compared with 94.45% for AutoHorizon, while requiring more VLA queries (14.0 versus 12.7). A similar pattern appears with π0 and H=50 (94.30% versus 94.05%, with 12.3 versus 10.6 queries).

These improvements are marginal, and the paper does not provide sufficient statistical evidence establishing a meaningful advantage over the strongest adaptive baseline.

Moreover, PAV requires an additional future-representation predictor and validity verifier, trained using collected rollout data. For the reported LIBERO configuration, this involves 6,000 collected episodes and approximately two million additional trainable parameters.

The real-world experiments report substantial gains, but compare PAV only against fixed-horizon baselines rather than other adaptive execution methods. In addition, Appendix E leaves several important details of the real-world evaluation protocol unspecified.

Finally, the threshold sensitivity analysis (Appendix C.2, Table 11) shows that average success changes considerably around the default threshold, from 85.65% at β=0.89 to 94.65% at β=0.90 and 89.45% at β=0.91. This raises additional concerns about the robustness of the horizon-selection criterion.

Overall, it is unclear whether the additional training and complexity of predictive verification are justified by a sufficiently consistent improvement over simpler adaptive execution strategies.

Questions for authors

Q1. Validity estimation.

Can the authors directly evaluate whether the learned validity scores correspond to actual successful-continuation probabilities? For example, evaluating multiple continuations from intermediate states reached by candidate prefixes would help validate the central definition in Eq. (4).

Q2. Advantage over adaptive execution baselines.

Can the authors provide statistical uncertainty and controlled success–query trade-off comparisons against AutoHorizon? Given the small improvements reported in Table 1, what practical advantage justifies the additional predictor, verifier, and training data?

Q3. Robustness and generalization.

How is the acceptance threshold selected, and how reliably does it transfer across tasks and environments? Can the authors explain the substantial performance variation observed in the threshold sweep and clarify whether similar sensitivity occurs in other settings?

7 comments

[W1,Q1] Validating Continuation Scores and Analyzing Recovery

Thank you for your comment. We agree that terminal-outcome supervision and overall performance gains alone do not sufficiently validate the learned validity score. A failed trajectory may contain recoverable intermediate states, so its final outcome cannot determine whether successful continuation remains possible after a given extension. Direct assessment requires multiple continuations from the same intermediate state, which is costly on physical robots and constrained by state restoration. We therefore used final success/failure outcomes for training, but the scores require independent validation. We added a branching evaluation in simulation that directly measures continuation success rates after candidate prefixes.

We randomly sampled states within each suite from episodes used for neither training nor model selection. We then selected states based solely on variation in continuation success rates across candidates or prefix lengths. This selection did not use verifier scores or their agreement with continuation outcomes. At each state, we computed scores for eight candidates before execution. We then restored the same state to execute each candidate prefix and performed eight continuations per candidate–length pair using a common FixedH10 continuation policy. We used the same repetition seeds, success criteria, and episode time limits throughout. Thus, the evaluation targets are newly measured success rates after each prefix, rather than terminal labels from existing trajectories. We separately assessed prefix and extension scores in three analyses.

Holding the starting state and prefix length fixed, we examined whether scores distinguish candidates with higher continuation success rates. Across 100 comparisons, the Spearman correlation between cumulative prefix scores and success rates over the eight candidates had a mean of 0.3383 and a median of 0.2943, indicating a positive rank association across candidates.

Holding the starting state and candidate fixed, we compared H10, H20, and H30 to examine whether scores reflect success-rate changes as more of the candidate is executed. Across 100 comparisons, the mean correlation was 0.7386, with a median of 0.8660. For one candidate in the Long suite, the prefix score decreased from 0.9271→0.8988→0.87740.9271 \to 0.8988 \to 0.8774 as execution length increased, while the success rate decreased from 8/8→7/8→4/88/8 \to 7/8 \to 4/8.

To assess local-score validity beyond the relationship between cumulative scores and execution length, we evaluated each additional five-action segment’s score. Holding the starting state and extension interval H→H+5H \to H+5 fixed, we computed the correlation across eight candidates between the local score and the change in success rate, Δp=psuccess(H+5)−psuccess(H)\Delta p = p_{\mathrm{success}}(H+5) - p_{\mathrm{success}}(H). Across 100 interval comparisons, the median correlation was 0.3853. For example, for an H15 →\to H20 extension in the Goal suite, a low-scoring candidate and the highest-scoring candidate both had a success rate of 4/8 before extension. After extension, the low-scoring candidate’s success rate decreased to 1/8, while the highest-scoring candidate’s remained at 4/8. The correlation across all eight candidates was 0.9262. This provides execution-based evidence that the local score is associated with whether executing an additional segment preserves or reduces the likelihood of success.

To examine recoverable intermediate states, we analyzed 30 episodes per method in which problems occurred during execution, including episodes that ultimately succeeded. Conditional retry, recovery, and final success rates follow.

\begin{array}{lrr} \text{Conditional rate} & \text{H10(Fixed)} & \text{PAV} \\ \hline \text{Retry given a problem} & 26/30 & 29/30 \\ \text{Actual recovery given a retry} & 21/26 & 25/29 \\ \text{Final success given a retry} & 14/26 & 20/29 \end{array}

Among episodes with a retry, PAV’s observed recovery rate was 86.2%, compared with 80.8% for FixedH10. Its final success rate was also higher, at 69.0% compared with 53.8%. Selecting shorter horizons when estimated success likelihood is low enables earlier observation and more responsive execution, which may contribute to the higher observed recovery rate.

Together, the branching results show that the learned scores reflect continuation success rates across candidates and execution lengths. They also track success-rate changes associated with individual extensions. We also interpret the length-normalized score in Eq. (14) as a score for horizon selection rather than a calibrated continuation probability. While these results do not establish numerical agreement between scores and success probabilities and were obtained using a FixedH10 continuation policy, they show that the scores track meaningful variation in observed continuation success rates. We will clarify this interpretation and supporting evidence in the paper.

[W2,Q3] Threshold Selection and Sensitivity

We apologize for not clearly describing the threshold selection procedure in the paper. For each sample, we used the minimum of its first two prefix scores as its representative score. Because the first horizon extension is a shared prerequisite for all subsequent extensions, this choice aims to calibrate the criterion for extending execution beyond the minimum length. We then selected the threshold using Kittler’s method, which approximates the score distribution with two Gaussians and minimizes the separation error. The resulting thresholds were 0.906771 for LIBERO–π0\pi_0–H50, 0.900278 for LIBERO–π0.5\pi_{0.5}–H10, 0.898986 for LIBERO–π0.5\pi_{0.5}–H50, and 0.907220 for RoboTwin–π0.5\pi_{0.5}–H32. To evaluate transferability across tasks and environments, we applied a common threshold of β=0.90\beta = 0.90 in all experiments. These results support the applicability of a shared threshold in the evaluated environments, but do not establish its optimality in every environment.

We additionally compared the unrounded shared, suite-specific, and task-specific thresholds on LIBERO–π0.5\pi_{0.5}–H50, as shown below. The suite-specific thresholds were 0.9123 for Spatial, 0.8961 for Object, 0.9147 for Goal, and 0.8892 for Long. Nevertheless, we acknowledge that threshold sensitivity is a limitation of our method.

\begin{array}{lrrrrrr} \text{Threshold setting} & \text{Spatial} & \text{Object} & \text{Goal} & \text{Long} & \text{Overall success rate} & \text{Average queries} \\ \hline \text{Shared Kittler }(\approx 0.899) & 97.0\% & 98.6\% & 91.8\% & 91.2\% & 94.65\% & 13.74 \\ \text{Suite-specific Kittler} & 96.8\% & 99.0\% & 91.4\% & 92.2\% & 94.85\% & 11.92 \\ \text{Task-specific Kittler} & 96.4\% & 98.4\% & 94.6\% & 93.0\% & 95.60\% & 12.38 \end{array}

This sensitivity can be understood through the trade-off between the temporal consistency of longer execution and the responsiveness of shorter execution. A lower threshold permits longer execution, but may delay necessary reactions, allowing errors to accumulate and leading to states from which success is difficult. We observed that this can also increase the frequency of h=5h=5 selection, as the system subsequently resorts to repeated short executions to compensate. Specifically, lowering β\beta from 0.90 to 0.88 increased the proportion of h≥20h \geq 20 selections from 21.88% to 42.92% and that of h=5h=5 selections from 24.99% to 36.59%, while reducing the success rate from 94.65% to 82.75%. Furthermore, the number of episodes in which a long execution (h≥20h \geq 20) was followed by low scores for h=5h=5 for at least three consecutive observation steps increased from 59 at the reference threshold (β≈0.899\beta \approx 0.899) to 97 at β=0.88\beta = 0.88. This is consistent with repeated short executions in states assessed as having a low likelihood of success after a long execution. It suggests that even frequent h=5h=5 selection may not prevent performance degradation if the system fails to respond when needed.

Conversely, a higher threshold imposes stricter conditions on execution extension. Although shorter execution provides responsiveness, it limits the benefits of temporal consistency and query reduction offered by longer execution. The method still selects some longer action chunks and outperforms fixed h=5h=5 execution, but appears unable to fully exploit these benefits. Specifically, at β=0.92\beta = 0.92, the h=5h=5 selection rate was 53.12%, and the average number of queries increased from 14.0 at β=0.90\beta = 0.90 to 25.1. The success rate decreased from 94.65% to 88.30%, although it remained above the 87.15% achieved with fixed h=5h=5 execution. These results are consistent with the trade-off discussed in the introduction. They highlight the importance of choosing a threshold that provides longer execution for consistency and shorter execution for responsiveness when each is needed.

[W2,Q2] Success–Query Trade-offs and Comparison with AutoHorizon

We agree that PAV sometimes requires more policy queries and that its success-rate improvements over AutoHorizon can be modest. To quantify variability across repeated evaluations, we evaluated PAV at β=0.90\beta=0.90 and AutoHorizon across three evaluation seeds. PAV achieved a mean success rate of 94.88% (±\pm 0.45%), compared with 94.47% (±\pm 0.58%) for AutoHorizon, where ±\pm denotes the standard deviation across seeds. The mean success-rate difference was 0.41 percentage points in favor of PAV. Moreover, as discussed in our response to Q3, suite-specific or task-specific thresholds can achieve both slightly higher success rates and fewer queries than AutoHorizon.

The optimal threshold may vary across tasks because the trade-off between responsiveness and temporal consistency is task-dependent. Tasks involving precise contact, sensitivity to small errors, or frequent environmental changes may benefit from a higher threshold. Conversely, tasks that require consistent execution over longer sequences, or where frequent replanning disrupts motion, may benefit from a lower threshold. This motivates the validation-based threshold selection procedure described in Q3, which allows the acceptance criterion to be adapted to the task or suite.

To further evaluate PAV against AutoHorizon beyond LIBERO, we also added a comparison on RoboTwin 2.0. The RoboTwin results reported in the AutoHorizon paper use policies fine-tuned separately for each task. For a fair comparison, we re-evaluated AutoHorizon using the same shared checkpoint as PAV, trained across RoboTwin tasks.

\begin{array}{lrrr} \text{Method} & \text{Success rate}\uparrow & \text{Average queries}\downarrow & \text{Average execution horizon} \\ \hline \text{PAV} & 58.72\% & 56.75 & 10.25 \\ \text{AutoHorizon (reimplementation)} & 45.64\% & 14.53 & 29.77 \end{array}

In this setting, AutoHorizon predominantly selects the maximum horizon of 32, yielding an average execution horizon of 29.77. This suggests limited effective adaptation under the shared-checkpoint setting. Its success rate of 45.64% is also close to the 45.40% achieved by fixed H32 execution. In contrast, PAV uses a shorter average execution horizon of 10.25 and achieves a success rate 13.08 percentage points higher, at the cost of more policy queries. Together with the LIBERO results, these findings support PAV’s effectiveness across benchmarks while showing that its success–query trade-off depends on the evaluation setting.

[W2] Clarifying Real-World Experimental Details

We will also fill in the TBD entries in Appendix E.1–E.2. Success is judged by a human evaluator. For Tray, success requires releasing the cube from the gripper and placing it correctly inside the tray. For Stack, the cubes must remain stacked without collapsing after the gripper releases the cube. For Button, the button must be pressed and produce an audible click. The maximum execution budget is 500 action steps per trial, with no separate wall-clock time limit.

For each task, we use the checkpoint obtained after 10,000 updates of full fine-tuning of π0.5\pi_{0.5}, and train each verifier for 60 epochs on 50 rollouts. The candidate horizons are {5,10,…,50}\{5,10,\ldots,50\}, the shared threshold is β=0.90\beta=0.90, and square-root block-count normalization is applied. Evaluation consists of 30 trials per task, separate from the training data, with initial object configurations matched across methods by episode index. Also, we apologize that time constraints during the rebuttal period prevent us from adding real-world comparisons with adaptive execution baselines.

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Paper summary

This paper proposes Policy-Aligned Predictive Verification (PAV), a method for adaptively selecting the execution horizon of action chunks generated by vision-language-action (VLA) policies. The method predicts future representations in the policy's task-conditioned feature space and estimates the validity of candidate action prefixes using trajectory-level success and failure supervision. A localization prior is introduced to avoid assigning failure-related penalties uniformly across an entire rollout.

Critical strengths
  1. The paper addresses an important problem in VLA deployment: balancing inference efficiency and feedback responsiveness when executing action chunks. Evaluating whether an action prefix preserves successful task completion is a useful alternative to relying solely on generation stability or prediction agreement.
  2. The policy-aligned prediction design is well motivated. By predicting future representations in the action-generating policy's feature space, the method attempts to retain task-relevant information for evaluating proposed actions.
  3. The experimental evaluation covers multiple simulation benchmarks, two VLA policies, and three real-world manipulation tasks. The results are promising, particularly when longer action chunks provide more opportunities for adaptive horizon selection.
Critical weaknesses
  1. Important experimental details remain incomplete, particularly in the real-world evaluation. Appendix E.1 still marks success criteria, timeout settings, verifier-training configurations, and parts of the evaluation procedure as TBD. These omissions make it difficult to assess the reliability and reproducibility of the reported real-world improvements.
  2. The validity of the learned local scores is not sufficiently established. Since individual action extensions have no direct validity labels, the verifier relies on terminal rollout outcomes and a localization prior to infer where validity is lost. The paper does not adequately demonstrate that these local scores reliably identify problematic action prefixes, which is central to the proposed method.
  3. Some baseline comparisons are not fully controlled. In the RoboTwin experiments, the fixed-horizon baseline is evaluated separately, so initial conditions are not guaranteed to be paired; the published DVAC results also follow a different evaluation protocol. Together with the relatively limited real-world evaluation across three tasks, this makes the generality of the reported improvements less convincing.
Questions for authors
  1. Could the authors clarify the missing real-world evaluation details, including task success criteria, timeouts, verifier-training configurations, and the procedure for matching initial conditions across methods?
  2. Can the authors provide direct evidence that the predicted local validity scores identify action prefixes that preserve successful task completion, beyond their correlation with terminal rollout outcomes?
  3. Could the authors provide a more controlled comparison with fixed-horizon baselines on RoboTwin 2.0, using matched initial conditions and consistent evaluation protocols where possible?
4 comments

[W2,Q2] Direct Validation of Local Scores Through Continuation Outcomes

Thank you for your helpful comment. We agree that training with terminal rollout outcomes and a localization prior alone does not sufficiently establish that the learned local scores identify problematic action extensions. To directly examine this, we repeatedly executed new continuations from intermediate states reached after candidate prefixes and evaluated whether their success rates and changes corresponded to the predicted scores.

We randomly sampled states within each suite from episodes used for neither training nor model selection. We then selected states based solely on variation in continuation success rates across candidates or prefix lengths. This selection did not use verifier scores or their agreement with continuation outcomes. This selection did not use verifier scores or their agreement with continuation outcomes. At each state, we computed scores for eight action candidates before execution, restored the same simulator state, and executed each prefix. We then performed eight continuation rollouts per candidate–length pair using a common FixedH10 continuation policy. Repetition seeds, success criteria, and episode time limits were identical across comparison conditions. Thus, these results validate the scores against newly measured continuation outcomes after each prefix, beyond their correlation with terminal labels from training trajectories.

Our primary analysis examined whether the local score of an additional five-action segment reflects the corresponding change in continuation success rate. For the same starting state and candidate, we computed the difference in continuation success rates between prefixes of length HH and H+5H+5, given by Δp=psuccess(H+5)−psuccess(H)\Delta p = p_{\mathrm{success}}(H+5) - p_{\mathrm{success}}(H). Holding the starting state and extension interval fixed, we then calculated the Spearman correlation between the segment’s local score and Δp\Delta p across eight candidates. Across 100 interval comparisons, the median correlation was 0.3853, indicating that higher local scores tended to correspond to more favorable changes in success rate.

For example, for an H15 →\to H20 extension in the Goal suite, a low-scoring candidate and the highest-scoring candidate both had a success rate of 4/8 before extension. After extension, the low-scoring candidate’s success rate decreased to 1/8, while the highest-scoring candidate’s remained at 4/8. The correlation across all eight candidates in this comparison was 0.9262. Similarly, for an H20 →\to H25 extension in the Object suite, a low-scoring candidate’s success rate decreased from 8/8 to 6/8, whereas the highest-scoring candidate’s increased from 3/8 to 6/8. The correlation across all eight candidates was 0.8225. These results provide direct execution-based evidence that local scores contain information useful for identifying individual extensions that reduce subsequent success rates, separately from cumulative prefix scores.

We also conducted two supporting analyses to assess whether cumulative prefix scores constructed from these local scores distinguish prefixes that preserve the possibility of successful task completion.

  • Comparing candidates at the same state and execution length, we evaluated the relationship between prefix scores and continuation success rates across eight candidates. Across 100 comparisons, the Spearman correlation had a mean of 0.3383 and a median of 0.2943, indicating a positive association with differences in success rates across candidates.
  • Comparing execution lengths for the same state and candidate, we evaluated prefix scores and success rates at H10, H20, and H30. Across 100 comparisons, the mean correlation was 0.7386, with a median of 0.8660. This supports that cumulative scores also reflect changes in success rate as more of the same candidate is executed.

Together, these results show that the learned scores help identify prefixes that preserve subsequent success likelihood and extensions that reduce it. This evidence goes beyond their association with the final outcomes of existing rollouts. Although evaluated using a FixedH10 continuation policy, the results provide evidence that the scores reflect meaningful variation in actual continuation success rates, including changes associated with individual action extensions. We will add this branching evaluation and clarify its interpretation in the paper to strengthen the empirical evidence for local-score validity.

[W1,Q1] Clarifying the Real-World Evaluation Protocol

Thank you for raising this important point. We did not sufficiently specify the real-world evaluation details in the submission and will add them to Appendix E.1–E.2. Success is judged by a human evaluator according to the following criteria. For Place Cube in Tray, the cube must be released from the gripper and correctly placed inside the tray. For Stack Cubes, the cubes must remain correctly stacked without collapsing after the gripper releases the cube. For Press Button, the button must be pressed and produce an audible click. The maximum execution budget is 500 action steps per trial, with no separate wall-clock time limit.

We will also clarify the training and execution settings. For each task, we use the checkpoint obtained after 10,000 updates of full fine-tuning of π0.5\pi_{0.5}, and train each verifier for 60 epochs on 50 rollouts. Across all tasks, we use candidate horizons {5,10,…,50}\{5,10,\ldots,50\}, a shared threshold of β=0.90\beta=0.90, and square-root block-count normalization. At each decision, we generate a single action chunk and execute the selected prefix without regenerating the chunk. Evaluation consists of 30 trials per task, separate from the training data. Initial object configurations are fixed by episode index to ensure matched initial conditions across methods. We will also specify that the total VLA query count includes the initial generation and that the average horizon is computed by assigning equal weight to every selected prefix.

[W3,Q3] Controlled Comparisons on RoboTwin 2.0

To address the potential mismatch in initial conditions, we conducted a controlled evaluation using 50 shared episodes for each of the 50 tasks in RoboTwin 2.0. We evaluated fixed-horizon baselines with h∈{4,8,20,32}h \in \{4,8,20,32\}, PAV, and our DVAC reimplementation. All methods used identical initial states, instructions, the Motus checkpoint, chunk length (H=32H=32), success criteria, and time limits. We verified that initial states and observations matched across methods at the start of every rollout. We report our DVAC reimplementation separately from the original paper’s published results, which use a different evaluation protocol.

The RoboTwin results reported in the AutoHorizon paper use policies fine-tuned separately for each task. For a fair comparison, we also implemented AutoHorizon using the same shared checkpoint trained across RoboTwin tasks. We evaluated it under the matched protocol described above. The table below compares PAV with both fixed-horizon baselines and adaptive execution methods.

\begin{array}{lrr} \text{Method} & \text{Success rate}\uparrow & \text{Average queries}\downarrow \\ \hline \text{Fixed H4} & 28.12\% & 135.87 \\ \text{Fixed H8} & 54.72\% & 54.50 \\ \text{Fixed H20} & 54.76\% & 20.69 \\ \text{Fixed H32} & 45.40\% & 14.39 \\ \text{DVAC (reimplementation)} & 45.60\% & 17.65 \\ \text{AutoHorizon (reimplementation)} & 45.64\% & 14.53 \\ \text{PAV (v4 + sqrt)} & 58.72\% & 56.75 \end{array}

Under matched evaluation conditions, PAV achieves the highest success rate among all evaluated methods. It exceeds the strongest fixed-horizon baseline by 3.96 percentage points, DVAC by 13.12 points, and AutoHorizon by 13.08 points, while requiring more queries than these baselines.

Dear Reviewer cDmV,

Thank you again for your thoughtful review and valuable feedback. We have carefully revised our rebuttal to address each of your comments and concerns.

As the discussion period is coming to an end, we would greatly appreciate it if you could take another look at our responses. If any part of our explanation remains unclear or if we have misunderstood any of your concerns, we would be sincerely grateful for the opportunity to provide further clarification.

Thank you again for your time and consideration.

Best, The Authors

Dear Reviewer cDmV,

Thank you for your thoughtful review and constructive feedback. Your comments helped us improve the reproducibility of the experiments and strengthen the direct evidence for the learned local scores.

To summarize the main additions and clarifications during the rebuttal,

  • We supplied the missing real-world evaluation details, including human-evaluated success criteria, a maximum budget of 500 action steps per trial, and no separate wall-clock time limit. We specified the policy checkpoints, verifier training for 60 epochs on 50 rollouts, and evaluation over 30 trials per task with initial object configurations matched across methods by episode index. We also clarified action-chunk execution and the aggregation of query counts and execution horizons.

  • We directly evaluated local scores using new continuations from intermediate states reached after candidate prefixes. Across 100 interval comparisons, the local scores of additional five-action segments had a median Spearman correlation of 0.3853 with the corresponding changes in continuation success rate. For example, in the Goal suite, a low-scoring extension reduced success from 4/8 to 1/8, while the highest-scoring extension preserved success at 4/8. These results provide execution-based evidence that local scores contain information useful for identifying problematic extensions.

  • Supporting analyses showed that cumulative prefix scores also reflect continuation outcomes. Across 100 comparisons, mean Spearman correlations were 0.3383 across candidates at a fixed length and 0.7386 across execution lengths for a fixed candidate. These analyses complement the local-score evaluation and go beyond correlations with terminal rollout labels.

  • We added controlled RoboTwin comparisons across 50 tasks using 50 shared episodes per task. Methods used identical initial states, instructions, the Motus checkpoint, chunk length, success criteria, and time limits. PAV achieved 58.72% success, compared with 54.76% for the strongest fixed-horizon baseline, 45.60% for our DVAC reimplementation, and 45.64% for our AutoHorizon reimplementation. These success-rate improvements required more queries. We explicitly distinguished the DVAC reimplementation from the original paper’s results obtained under a different protocol.

We will incorporate these experiments and procedural details into the revised paper. We will also clarify that the continuation analysis uses a FixedH10 follow-up policy, that the real-world evaluation covers three tasks, and that the RoboTwin gains involve a success–query trade-off. The use of default AutoHorizon hyperparameters will be explicitly stated when interpreting the comparison.

Thank you again for helping us strengthen the experimental evidence and reproducibility of this work.

Comments on the paper

2 comments

Dear Reviewers,

Thank you again for your time and thoughtful feedback throughout the review process. We have provided additional experiments and clarifications in our responses and follow-up replies.

As the discussion period is nearing its end, please let us know if you have any remaining questions or feel that any concern has not been fully addressed. We would be happy to provide further clarification before the discussion closes.

Best regards, The Authors

Dear Area Chair and Reviewers,

Thank you for your time and constructive feedback. As the discussion closes, we summarize the additional evidence provided during the rebuttal and the status of each review thread.

Additional experiments and clarifications

  • We directly validated the learned scores against success rates measured through new continuations after candidate prefixes. Across 100 comparisons per analysis, cumulative prefix scores had mean Spearman correlations of 0.3383 with success rates across candidates and 0.7386 across execution lengths. Local extension scores had a median correlation of 0.3853 with changes in success rate, providing direct evidence beyond terminal rollout labels.

  • Among episodes with a retry, PAV’s observed recovery rate was 86.2%, compared with 80.8% for FixedH10. Final success rates were 69.0% and 53.8%, respectively.

  • We clarified Kittler threshold selection and analyzed threshold sensitivity. Suite-specific and task-specific thresholds were selected exclusively on validation data and fixed before evaluation. Across three LIBERO seeds, suite-specific PAV achieved 95.13% ±\pm 0.48% success with 11.98 ±\pm 0.13 queries, compared with 94.47% ±\pm 0.58% and 13.03 ±\pm 0.31 queries for AutoHorizon. Here, ±\pm denotes the standard deviation across seeds. PAV achieved higher mean success with fewer queries.

  • We conducted controlled RoboTwin comparisons across 50 tasks with 50 shared episodes per task, matching initial conditions, instructions, checkpoint, chunk length, success criteria, and time limits. PAV achieved 58.72% success, compared with 54.76% for the best-performing fixed-horizon baseline, 45.60% for our DVAC reimplementation, and 45.64% for our AutoHorizon reimplementation. These gains required more queries than those baselines.

  • We supplied the missing real-world evaluation and training details, including initial-condition matching, query aggregation, and sequential execution and inference. We confirmed that both original and rerun RoboTwin experiments used β=0.90\beta=0.90 and will correct the typo in Appendix B.

Status of the review discussions

  • Reviewer cDmV assigns a score of 3, Weak Acceptance, with confidence 3. We provided responses to each of their three concerns, including the real-world protocol details, direct local-score validation, and controlled RoboTwin comparisons. We have not yet received a follow-up.

  • Reviewer H7i8 assigns a score of 3, Weak Acceptance, with confidence 4. H7i8 confirmed that their main concerns were largely addressed, particularly by direct score validation and results across seeds, and raised their rating to Weak Acceptance. They requested explicit discussion of threshold sensitivity and default AutoHorizon settings as limitations.

  • Reviewer Bhet assigns a score of 2, Weak Rejection, with confidence 2, and provided a positive follow-up. Bhet acknowledged that the additional evidence substantially addressed threshold-selection concerns and provided useful direct evidence for the verifier’s scores. We answered their three follow-up questions on seed variability, validation-only threshold selection, and AutoHorizon hyperparameters, and have not yet received a further update.

We will incorporate these results and clarifications into the revised paper. We will explicitly discuss threshold sensitivity, validation-selected PAV thresholds versus default AutoHorizon settings, and the scope of the FixedH10 continuation evaluation. We will also clarify the success–query trade-offs and the remaining limitations of the real-world evaluation.

We hope this summary assists your final assessment. Thank you again for helping us strengthen the paper.

Best regards, The Authors

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