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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
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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.
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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
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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.
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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.
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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.
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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
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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.
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What evidence distinguishes semantic grounding failures from physical execution failures in the constituent models? Are the proposed task categories supported by systematic failure annotations?
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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?
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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?
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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
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.
| Method | Mean T across domains | 95% task-bootstrap interval |
|---|---|---|
| Pearson (primary) | 0.052 | [−0.002, 0.146] |
| Spearman ranks | 0.063 | [0.013, 0.121] |
| Two-way centering | 0.145 | [0.015, 0.250] |
| Logistic ability–difficulty residuals | 0.154 | [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.
| Task | Clean 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.
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.
| Domain | Improved / worse / tied tasks | Median task difference | Tasks gaining ≥5 pp | Mean gain and 95% task-bootstrap interval |
|---|---|---|---|---|
| Clean | 28 / 10 / 12 | +1 pp | 13 | +1.66 pp [−1.14, 4.54] |
| Random | 32 / 8 / 10 | +3 pp | 20 | +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.
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.
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.
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.