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Under review as a conference paper at ICLR 2027

WARM: A World Action Rectification Model Unifying VLA and WAM through a Planning-Rectification Architecture

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Abstract

Vision-Language-Action (VLA) models map instructions and images to actions and are strong at semantic planning, but relatively weak at contact-precise, physics-grounded control. World Action Models (WAMs) jointly generate future video and future actions, internalizing a physical forward model that can rectify motion, yet they struggle with long-horizon language planning. We show that the two families are complementary rather than competing: on 50 RoboTwin bimanual tasks they are only moderately correlated (Spearman ), each owns a disjoint set of signature successes, and the per-task oracle reaches , strictly above either family alone. We propose WARM (World Action Rectification Model), which unifies them through a plan-then-rectify architecture analogous to the cerebrum–cerebellum split: a frozen VLA plans a nominal trajectory , which is treated as an SDEdit prior and rectified by a flow-matching WAM. Ablations show that planning must come from the VLA (letting the WAM plan for itself drops success from to ), and that among coupling schemes (joint, joint_full, parallel, clamp), clamp—evaluate the plan while the video branch generates, then refine—is best. WARM attains on RoboTwin, improving over both the VLA () and WAM () baselines.

Primary area:
applications to robotics, autonomy, planning
Keywords:
vision-language-action models, world models, world action models, robot manipulation, embodied AI, flow matching, generative models, SDEdit

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 3 reviews, above 27% of the others.
Reviewer_dHx4OpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper presents WARM, which combines a pretrained VLA planner with a pretrained World Action Model at inference time. The VLA proposes an action chunk, which is perturbed to an intermediate noise level and refined through coupled video-action denoising. The preferred clamp schedule holds the noisy action proposal fixed during early video denoising, then releases it for joint refinement. Using LingBot-VLA and Motus, WARM achieves 90.32% and 90.70% success on the clean and randomized RoboTwin settings, respectively. The paper also analyzes task-level complementarity between VLA and WAM checkpoints and compares initialization and coupling strategies.

Critical strengths
  1. The method improves both constituent models without additional joint training. Across 50 tasks with 100 evaluation episodes per task and setting, WARM exceeds LingBot-VLA and Motus in aggregate. This makes inference-time refinement a practically interesting alternative to retraining a unified model.

  2. Clamp outperforms parallel denoising, while performance peaks at intermediate noise levels. These findings provide useful evidence that preserving part of the original proposal matters when composing the policies.

Critical weaknesses
  1. The central contribution of video-based physical reasoning is not isolated. Schedule, noise, and initialization ablations do not remove or disrupt video-to-action interaction under a matched refinement procedure. The improvement may therefore reflect the WAM’s action prior or additional inference computation rather than transferable physical reasoning specifically enabled by video prediction.

  2. Task-level success differences and moderate rank correlations establish heterogeneous performance, but do not identify the reason for that heterogeneity. Different training data, model capacities, or checkpoint quality could also produce these patterns. The analysis therefore does not substantiate the broader claim that VLAs provide semantic planning while WAMs provide physical correction.

  3. The demonstrated benefit is limited to one model pairing, and its incremental magnitude needs better characterization. Actual refinement uses LingBot-VLA and Motus only. Self-clamp already achieves 89.1%, compared with 90.3% for VLA-guided clamp, and uncertainty for this difference is not reported. The stronger standalone WAM results listed in Section 4.1 also make it important to distinguish improvement over selected constituents from a broader advance in policy performance.

  4. WARM executes both a VLA and a coupled video-action model at inference time, but does not report latency, memory consumption, or a comparison at matched computation. These measurements are consequential because a modest success-rate gain may have different practical value depending on the resulting control frequency and resource requirements.

Questions for authors
  1. Under the same action initialization and denoising schedule, what happens when video-to-action interaction is disabled or video conditioning is disrupted? This comparison would directly affect my assessment of the proposed physical-refinement mechanism.

  2. What evidence distinguishes semantic grounding failures from physical execution failures in the constituent models? Are the proposed task categories supported by systematic failure annotations?

  3. Can the paper provide paired outcome statistics and uncertainty for clamp versus self-clamp and Motus? Is the improvement distributed across tasks or concentrated in a small subset?

  4. What are the complete pipeline’s latency, memory consumption, denoising budget, and resulting control frequency? How does its success compare with alternatives under a matched inference budget?

  5. How is the original variant’s action initialization reconciled with its timestep schedule, and what exactly changes in the “without SDE” variants? Were the default noise level and coupling schedule selected on data separate from the reported evaluation episodes?

6 comments
AuthorsOpenReview ↗

Response to Reviewer dHx4 (1/5): video ablation and inference cost

We thank the reviewer for the detailed questions.

Q1: Disrupting video conditioning under the refinement protocol.

We added a disrupted-video condition to address your Q1: the observed frame is retained, future-video latents remain at their initial Gaussian noise, and the video timestep is held at 1 without integrating the video velocity. We retain the action-initialization protocol, clamp action schedule, nominal t₀=0.6, and ten model forward calls, with no additional training.

ConditionCleanRandom
Full WARM90.32% (4516/5000)90.70% (4535/5000)
Frozen future-video denoising88.64% (4432/5000)86.54% (4327/5000)
Full minus frozen+1.68 pp+4.16 pp
95% task-bootstrap interval[−0.16, 3.64] pp[2.30, 6.12] pp

Each setting covers all 50 tasks with 100 episodes per task. Task identities, scene seeds, and instructions match the historical full-video baseline. Intervals use 10,000 task-level bootstrap samples. These results support an incremental contribution from iterative future-video denoising in this model pair, particularly under randomization. The Clean interval includes zero, so we do not claim a robust positive effect across task resampling there.

Q4: Pipeline cost and denoising budget.

We measured all three policies on the same A800 80GB GPU and repeated the comparison on an A100 80GB. Each method and hardware setting uses 60 synchronous closed-loop episodes: six tasks, two domains, and five shared seeds.

MethodA800 P50/P95 (s)A100 P50/P95 (s)A800 replans/sA800 peak memory (GiB)
LingBot-VLA1.29 / 6.981.34 / 8.980.20316.7
Motus2.78 / 3.072.89 / 3.150.22549.2
WARM2.92 / 3.133.00 / 8.580.21958.0

Latency spans observation acquisition to chunk readiness, excluding only the first chunk of each task–setting worker. Device memory includes the simulator. Execution is synchronous: VLA executes up to 50 actions per chunk and Motus/WARM up to 16. VLA and Motus each use ten sampling steps; WARM uses ten VLA proposal steps plus ten Motus refinement steps. Replanning rates include simulator execution and are not low-level control frequencies.

WARM adds 0.11–0.14 s in median latency over native Motus, about 4–5%, and 8.8 GiB in A800 peak memory. Native Motus and WARM differ in caching and video decoding, so this is a deployment-level comparison, not an isolated measure of added VLA computation. We have not measured success under a matched inference budget.

AuthorsOpenReview ↗

Response to Reviewer dHx4 (2/5): task-profile differences and failure attribution

Q2: Semantic grounding versus physical execution.

We agree that task-success differences do not directly identify semantic-grounding versus physical-execution failures. The original family-level division of capabilities was too strong.

We expanded the published task-wise analysis to ten VLAs and ten video-backbone WAMs, requiring the full RoboTwin 2.0 protocol (50 Clean plus 500 randomized demonstrations per task, multi-task training) and complete results for 50 tasks in both domains, yielding 2,000 entries. These are author-reported public results, not local reproductions of twenty models, and the models are not assumed to have independent lineages.

To reduce differences in overall ability, we first center each model's task-success profile: uₘₜ=pₘₜ−meanₜ(pₘₜ). We compare within-family and cross-family task-profile correlations using T=½ mean(ρ_VV)+½ mean(ρ_WW)−mean(ρ_VW), with separate means over the 45 VLA–VLA, 45 WAM–WAM, and 100 cross-family pairs. The 190 overlapping model pairs are not treated as independent observations.

Centering removes additive ability differences but does not eliminate ceiling/floor effects. We therefore additionally examine Spearman task ranks, correlations after removing model and common-task means, and standardized residual correlations from a family-blind logistic ability–difficulty baseline, logit(qₘₜ)=αₘ+βₜ. We use 5,000 synchronized task-bootstrap samples across all models and both domains, refitting the logistic baseline each time. Intervals condition on this model cohort.

MethodMean T across domains95% task-bootstrap interval
Pearson (primary)0.052[−0.002, 0.146]
Spearman ranks0.063[0.013, 0.121]
Two-way centering0.145[0.015, 0.250]
Logistic ability–difficulty residuals0.154[0.025, 0.245]

The primary Pearson interval includes zero, while the supplementary analyses show positive structure. Omitting any one of the twenty models preserves positive point estimates for all four measures. In the raw correlations, WAM–WAM similarity is higher than cross-family similarity, whereas VLA–VLA similarity is not; we do not claim equally tight clusters for both families.

For concrete task preferences, let Dₜ=mean_VLA(uₘₜ)−mean_WAM(uₘₜ): positive values indicate relative VLA preference and negative values relative WAM preference. The following are the top three and bottom three tasks ranked by D averaged across domains; they are descriptive examples, not per-task significance claims.

TaskClean D (pp)Random D (pp)
stack_bowls_three+8.59+8.95
place_dual_shoes+3.59+8.75
place_empty_cup+5.89+5.45
hanging_mug-12.31-9.45
click_bell-18.01-23.65
click_alarmclock-16.31-26.85

The sign of D agrees across domains for 41 of 50 tasks. This concerns family-mean contrasts, not every cross-family model pair. Reusing 300 task-demand ratings from three language-model judges and two rounds per task did not support the hypothesized semantic/execution division in a joint regression. Our conclusion from this analysis is therefore limited: these models exhibit family-associated task-profile structure on RoboTwin. Together with WARM's improvements over its constituents, this supports empirical complementarity, but not a strict semantic-versus-physical decomposition or a causal architecture effect independent of training, capacity, and implementation.

Model roster. VLAs: ACE-Ego-0, Galaxea-G0.5, HyVLA-0.5, JoyAI-RA-0.1, LingBot-VLA (without depth), Qwen3-VL-OFT, RotVLA, X-VLA, π0, and π0.5. WAMs: AHA-WAM, Efficient-WAM, Fast-WAM, FlowWAM, GigaWorld-Policy, Light-WAM, LingBot-VA, OSWAM, WING, and X-WAM. π0 refers to its reported full-data multi-task result, not the Clean-only single-task RoboTwin baseline.

AuthorsOpenReview ↗

Response to Reviewer dHx4 (3/5): uncertainty and distribution of task gains

Regarding dHx4 Q3, episode-paired records for clamp and the final self-clamp result were not retained. We therefore cannot provide reliable paired win/loss counts or a paired significance claim for that comparison. The point-estimate difference between 90.3% and 89.1% is modest, and we interpret this difference cautiously.

For WARM versus Motus, Table 2 reports task-level success rates and displays only a subset of tasks. We recovered the complete fifty-task table and computed task-wise differences and uncertainty. These are not same-scene episode-paired outcomes: Motus task rates come from published reports, so we do not present this as an episode-paired test.

DomainImproved / worse / tied tasksMedian task differenceTasks gaining ≥5 ppMean gain and 95% task-bootstrap interval
Clean28 / 10 / 12+1 pp13+1.66 pp [−1.14, 4.54]
Random32 / 8 / 10+3 pp20+3.68 pp [1.40, 6.08]

The gains are not uniform. On Clean, the five largest positive-gain tasks account for 57.8% of the gross positive gains; removing them gives a mean difference of −0.56 pp on the other 45 tasks. On Random, the five largest gains account for 43.2% of gross positive gains, and the remaining tasks still average +1.82 pp. Thus, the Clean improvement is more concentrated, whereas the Random improvement is more broadly distributed. We do not claim improvement on every task.

For example, handover_mic improves by 20/35 pp on Clean/Random and place_a2b_left by 8/16 pp. Regressions also occur, including −6 pp for handover_block on Clean. The next comment provides the full fifty-task table, including regressions and ties.

The comparator is the complete fifty-task vector from Table 14 of the original Motus paper. Its recomputed means are 88.66%/87.02% on Clean/Random, matching the submitted overall comparison. Intervals use 10,000 bootstrap samples over the fifty tasks.

Reviewer_gHjWOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces WARM, which combines a frozen VLA and a frozen WAM at inference time. The VLA proposes actions, and the WAM refines them using predicted future video. The implementation uses LingBot-VLA to generate an action proposal, adds noise to it, and applies Motus to jointly denoise video and actions. Among the coupling schedules evaluated, clamp performs best. It initially holds the noisy action proposal fixed while denoising video, then jointly refines both. WARM outperforms both constituent models across 50 RoboTwin 2.0 tasks under the Clean and Random settings. The authors attribute these gains to complementary semantic planning and physical prediction capabilities.

Critical strengths
  1. Combining frozen models at inference time improves task success. WARM offers a straightforward way to combine existing VLA and WAM models through action initialization and sampling schedules, without additional training. It improves success rates over both constituent models on RoboTwin 2.0.
  2. The coupling ablations identify an effective refinement schedule. The experiments compare several video and action denoising schedules and find clamp to be the most effective. This schedule first holds the noisy VLA proposal fixed while predicting its visual consequences, then allows joint denoising to refine the actions.
Critical weaknesses
  1. Evidence for a general division of capabilities between VLAs and WAMs remains limited. Although Section 4.1 acknowledges that complementarity depends on the model pair, the analysis does not rule out the effects of differences in training data, model size, and training methods. It also lacks comparisons between pairs of VLAs or pairs of WAMs. The results therefore do not establish that VLAs generally excel at semantic planning while WAMs excel at physical execution. I suggest adding pairwise comparisons within each model family and narrowing the claims accordingly.
  2. Inference cost and deployment feasibility are insufficiently evaluated. WARM runs VLA action generation followed by WAM refinement, but reports neither inference latency nor update frequency and provides no real robot validation. This makes it difficult to assess the tradeoff between success rate and latency. I suggest comparing WARM and its constituent models on the same hardware and reporting the action chunk length, the number of actions executed per update, and whether execution is synchronous or asynchronous.
Questions for authors
  1. Figure 1(b) shows a case where the standalone WAM selects the wrong target, whereas WARM selects the correct target and succeeds. Could the authors also show the original VLA action proposal for this case and explain how its target choice is preserved during WAM refinement, as well as which execution details are modified?
  2. What is the end-to-end latency of VLA proposal generation followed by WAM refinement, and what action chunk update or replanning frequency does WARM achieve? Please specify the hardware, the denoising steps for both models, the number of actions executed per chunk, and whether execution is synchronous or asynchronous.
  3. In Table 3, the success rate of joint is reported as 48–64% at a fixed (t_0=0.6), while the other methods have single values. Could the authors clarify what this range represents and the evaluation settings used to obtain it?
3 comments
AuthorsOpenReview ↗

Response to Reviewer gHjW (1/2): task-profile structure and Figure 1(b)

We thank the reviewer.

Within-family comparisons and scope of the capability claim.

We agree that task-success differences do not directly identify semantic-grounding versus physical-execution failures. The original family-level division of capabilities was too strong.

We expanded the published task-wise analysis to ten VLAs and ten video-backbone WAMs, requiring the full RoboTwin 2.0 protocol (50 Clean plus 500 randomized demonstrations per task, multi-task training) and complete results for 50 tasks in both domains, yielding 2,000 entries. These are author-reported public results, not local reproductions of twenty models, and the models are not assumed to have independent lineages.

To reduce differences in overall ability, we first center each model's task-success profile: uₘₜ=pₘₜ−meanₜ(pₘₜ). We compare within-family and cross-family task-profile correlations using T=½ mean(ρ_VV)+½ mean(ρ_WW)−mean(ρ_VW), with separate means over the 45 VLA–VLA, 45 WAM–WAM, and 100 cross-family pairs. The 190 overlapping model pairs are not treated as independent observations.

Centering removes additive ability differences but does not eliminate ceiling/floor effects. We therefore additionally examine Spearman task ranks, correlations after removing model and common-task means, and standardized residual correlations from a family-blind logistic ability–difficulty baseline, logit(qₘₜ)=αₘ+βₜ. We use 5,000 synchronized task-bootstrap samples across all models and both domains, refitting the logistic baseline each time. Intervals condition on this model cohort.

MethodMean T across domains95% task-bootstrap interval
Pearson (primary)0.052[−0.002, 0.146]
Spearman ranks0.063[0.013, 0.121]
Two-way centering0.145[0.015, 0.250]
Logistic ability–difficulty residuals0.154[0.025, 0.245]

The primary Pearson interval includes zero, while the supplementary analyses show positive structure. Omitting any one of the twenty models preserves positive point estimates for all four measures. In the raw correlations, WAM–WAM similarity is higher than cross-family similarity, whereas VLA–VLA similarity is not; we do not claim equally tight clusters for both families.

For concrete task preferences, let Dₜ=mean_VLA(uₘₜ)−mean_WAM(uₘₜ): positive values indicate relative VLA preference and negative values relative WAM preference. The following are the top three and bottom three tasks ranked by D averaged across domains; they are descriptive examples, not per-task significance claims.

TaskClean D (pp)Random D (pp)
stack_bowls_three+8.59+8.95
place_dual_shoes+3.59+8.75
place_empty_cup+5.89+5.45
hanging_mug-12.31-9.45
click_bell-18.01-23.65
click_alarmclock-16.31-26.85

The sign of D agrees across domains for 41 of 50 tasks. This concerns family-mean contrasts, not every cross-family model pair. Reusing 300 task-demand ratings from three language-model judges and two rounds per task did not support the hypothesized semantic/execution division in a joint regression. Our conclusion from this analysis is therefore limited: these models exhibit family-associated task-profile structure on RoboTwin. Together with WARM's improvements over its constituents, this supports empirical complementarity, but not a strict semantic-versus-physical decomposition or a causal architecture effect independent of training, capacity, and implementation.

Model roster. VLAs: ACE-Ego-0, Galaxea-G0.5, HyVLA-0.5, JoyAI-RA-0.1, LingBot-VLA (without depth), Qwen3-VL-OFT, RotVLA, X-VLA, π0, and π0.5. WAMs: AHA-WAM, Efficient-WAM, Fast-WAM, FlowWAM, GigaWorld-Policy, Light-WAM, LingBot-VA, OSWAM, WING, and X-WAM. π0 refers to its reported full-data multi-task result, not the Clean-only single-task RoboTwin baseline.

Q1: Original VLA proposal in Figure 1(b). We agree that a matched visualization of the original proposal would be informative. We do not currently provide that matched visualization for this case, so Figure 1(b) alone does not establish exactly which proposal details were preserved or corrected. We interpret it as an illustration of the observed outcome rather than direct trajectory-level evidence of semantic preservation and physical correction.

AuthorsOpenReview ↗

Response to Reviewer gHjW (2/2): inference cost and Table 3 correction

Q2: Hardware, latency, and update frequency.

We measured all three policies on the same A800 80GB GPU and repeated the comparison on an A100 80GB. Each method and hardware setting uses 60 synchronous closed-loop episodes: six tasks, two domains, and five shared seeds.

MethodA800 P50/P95 (s)A100 P50/P95 (s)A800 replans/sA800 peak memory (GiB)
LingBot-VLA1.29 / 6.981.34 / 8.980.20316.7
Motus2.78 / 3.072.89 / 3.150.22549.2
WARM2.92 / 3.133.00 / 8.580.21958.0

Latency spans observation acquisition to chunk readiness, excluding only the first chunk of each task–setting worker. Device memory includes the simulator. Execution is synchronous: VLA executes up to 50 actions per chunk and Motus/WARM up to 16. VLA and Motus each use ten sampling steps; WARM uses ten VLA proposal steps plus ten Motus refinement steps. Replanning rates include simulator execution and are not low-level control frequencies.

WARM adds 0.11–0.14 s in median latency over native Motus, about 4–5%, and 8.8 GiB in A800 peak memory. Native Motus and WARM differ in caching and video decoding, so this is a deployment-level comparison, not an isolated measure of added VLA computation. We have not measured success under a matched inference budget.

Q3: The 48–64 entry.

Thank you for identifying the problem in Table 3. The 48–64 range was an exploratory placeholder that we failed to replace with a single measurement under the final configuration before submission. This was our oversight; the range is not a confidence interval and should not be interpreted as uncertainty at a fixed t₀.

We have completed the missing evaluation using the same continued-training Motus checkpoint, joint, t₀=0.6, ten steps, and all 50 Clean tasks with 100 episodes each. The result is 4473/5000 = 89.46%, reported as 89.5% in Table 3 of the corrected PDF. Clamp achieves 90.32%, a difference of 0.86 percentage points. The corrected PDF also removes the word “substantially” from that comparison: the corrected result gives clamp a higher point estimate in this configuration, but does not support the large separation suggested by the placeholder. This evaluation provides a new auditable result rather than reconstructing the provenance of the exploratory range. We apologize for the error and the resulting confusion.

Thank you for the detailed additional analyses and latency measurements, and for correcting Table 3. These responses clarify several important issues.

I appreciate the narrower claim about empirical complementarity. However, the additional analysis does not support the proposed division between semantic planning and physical execution, which was central to the paper’s motivation and interpretation. While combining complementary models remains a reasonable approach, the specific mechanism used to explain WARM’s gains remains insufficiently supported.

The latency measurements address the reporting gap, but my concern about practical deployment remains. WARM still requires approximately three seconds to produce an action chunk. Without real robot validation or an evaluation of the effects of this delay on closed-loop performance, the practical benefit remains unclear.

I acknowledge the authors’ efforts and clarifications, but these remaining concerns lead me to maintain my rating.

Reviewer_mMZSOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

WARM combines a frozen VLA with a frozen world-action model at inference time. The VLA proposes a low-level action chunk, which is partially noised and refined through coupled video/action generation. The preferred clamp schedule holds the noisy action proposal fixed during early video denoising and then releases both branches for joint refinement. Instantiated with LingBot-VLA and Motus, the method improves average success over its two components on 50 RoboTwin 2.0 tasks. The paper interprets this as complementary semantic planning and physical refinement.

Critical strengths
  1. The training-free reuse of pretrained models is an appealing direction. The proposed procedure offers a concrete way to combine an existing action proposal with a generative world-action model without retraining either component.

  2. Evaluation across 50 tasks and comparisons of coupling schedules, noise levels, and self-clamp provide useful evidence that the particular composition can improve over its constituent models. The schedule ablations are informative for designing inference-time model combinations.

Critical weaknesses
  1. The evidence supports the effectiveness of the composition more clearly than the proposed mechanism. The schedule and initialization ablations are useful, but do not clearly distinguish video-based physical correction from refinement under Motus’s learned action prior. Self-clamp already achieves 89.1% versus clamp’s 90.3% on Clean, suggesting that the stronger claim that semantic planning must remain with the VLA needs qualification. The authors appropriately acknowledge that complementarity is pair-dependent; nevertheless, the actual refinement is demonstrated only with LingBot-VLA and Motus, so the broader claim of transferable physical reasoning remains insufficiently established.

  2. The practical performance–cost trade-off remains unclear. WARM improves over both components, including meaningful gains under randomization (+1.66/+3.68 percentage points over Motus on Clean/Random). However, it requires running both pretrained models, and no end-to-end latency or compute comparison is reported. This makes it difficult to assess when the improvement justifies the added system complexity. This concern is about practical value, not a requirement to outperform every standalone model.

Questions for authors
  1. What evidence distinguishes the proposed transfer of physical reasoning through video prediction from refinement under Motus’s learned action prior? The existing schedule ablations support the method’s effectiveness, but clarifying this distinction would help assess the central mechanistic claim.

  2. What is the end-to-end inference cost relative to LingBot-VLA and Motus? This would help interpret the practical value of the reported gains.

1 comment
AuthorsOpenReview ↗

Response to Reviewer mMZS

We thank the reviewer for the constructive feedback.

Q1: Contribution of future-video denoising.

We added a disrupted-video condition to address your Q1: the observed frame is retained, future-video latents remain at their initial Gaussian noise, and the video timestep is held at 1 without integrating the video velocity. We retain the action-initialization protocol, clamp action schedule, nominal t₀=0.6, and ten model forward calls, with no additional training.

ConditionCleanRandom
Full WARM90.32% (4516/5000)90.70% (4535/5000)
Frozen future-video denoising88.64% (4432/5000)86.54% (4327/5000)
Full minus frozen+1.68 pp+4.16 pp
95% task-bootstrap interval[−0.16, 3.64] pp[2.30, 6.12] pp

Each setting covers all 50 tasks with 100 episodes per task. Task identities, scene seeds, and instructions match the historical full-video baseline. Intervals use 10,000 task-level bootstrap samples. These results support an incremental contribution from iterative future-video denoising in this model pair, particularly under randomization. The Clean interval includes zero, so we do not claim a robust positive effect across task resampling there.

Q2: End-to-end inference cost.

We measured all three policies on the same A800 80GB GPU and repeated the comparison on an A100 80GB. Each method and hardware setting uses 60 synchronous closed-loop episodes: six tasks, two domains, and five shared seeds.

MethodA800 P50/P95 (s)A100 P50/P95 (s)A800 replans/sA800 peak memory (GiB)
LingBot-VLA1.29 / 6.981.34 / 8.980.20316.7
Motus2.78 / 3.072.89 / 3.150.22549.2
WARM2.92 / 3.133.00 / 8.580.21958.0

Latency spans observation acquisition to chunk readiness, excluding only the first chunk of each task–setting worker. Device memory includes the simulator. Execution is synchronous: VLA executes up to 50 actions per chunk and Motus/WARM up to 16. VLA and Motus each use ten sampling steps; WARM uses ten VLA proposal steps plus ten Motus refinement steps. Replanning rates include simulator execution and are not low-level control frequencies.

WARM adds 0.11–0.14 s in median latency over native Motus, about 4–5%, and 8.8 GiB in A800 peak memory. Native Motus and WARM differ in caching and video decoding, so this is a deployment-level comparison, not an isolated measure of added VLA computation. We have not measured success under a matched inference budget.

We also acknowledge that the clamp/self-clamp difference (90.3% versus 89.1%) is modest and does not establish that semantic planning must universally reside in a VLA. Our interpretation is limited to empirical complementarity in the evaluated composition.

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

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