- Rating
- 3
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
This paper proposes Struct-DPO to align video-based robot policies using structural preferences between generated videos and their corresponding environment executions. It combines depth reprojection, edge alignment, and spatial displacement for preference selection, with hindsight relabeling for failed episodes. Experiments show improvements on RoboCasa and a physical robot, but stronger controls and more consistent reporting are needed.
Critical strengths
1,Environment-executed rollouts provide a practical source of preference supervision without manual preference annotation. 2,The method evaluates downstream task success, including encouraging real-robot improvements from 52% to 82% in the single-task setting. 3,Component ablations, phase-wise execution analysis, and failure cases provide useful insights.
Critical weaknesses
1,The structural metrics do not isolate physical violations. Differences between generated and executed videos can also arise from action-decoder errors, timing offsets, or appearance changes. In particular, same-timestep RAFT displacement measures spatial disagreement rather than temporal dynamics. Independent contact or object-motion evaluation is needed to support the interpretation of these errors as physical inconsistency.
2,The paper could broaden its discussion of structural grounding to include OccScene: Semantic Occupancy-based Cross-task Mutual Learning for 3D Scene Generation, ORV: 4D Occupancy-centric Robot Video Generation, and OmniNWM: Omniscient Driving Navigation World Models. These provide relevant perspectives on occupancy-based generation, downstream policy benefits, and geometry-grounded rewards, respectively. Discussing their supervision requirements and the distinction between explicit structural representations and preference-based alignment would sharpen the paper’s positioning.
3, Since training includes an SFT term on environment observations, the gains may partly come from additional supervised adaptation. Please compare against LoRA-SFT on the same observations and DPO with randomly selected pairs, using matched data sizes and optimization budgets. Metric-removal ablations should also control the number of selected pairs.
4,The main simulation improvement is 52.46% to 55.65%, corresponding to 22 additional successes over 690 trials; five tasks deteriorate. Please report paired confidence intervals and variability across training seeds. These results support an average improvement, but not uniformly improved performance across tasks.
Questions for authors
1,Section 4.3 states 50 evaluation runs, but Table 4 reports 65% success, which cannot arise from a single set of 50 binary outcomes. Please provide success counts and explain any averaging.
2,Table 7 states 20 demonstrations per task but reproduces Struct-DPO’s 55.65% result from the 30-trial protocol. Were all methods evaluated on identical episodes? Please also reconcile the different baseline subsets used in Tables 5 and 6.
3,The real-world subset and all-pair variants use 102 and 951 optimization steps. A shared training-loss stopping rule does not eliminate this confound; please provide a matched-budget comparison.
We thank the reviewer for the detailed review.
W1. Not isolating physical violations
We partially agree with the reviewer's concerns regarding the interpretation of our structural metrics.
Discrepancies between generated and executed videos can arise not only from physical violations but also from action-decoder errors and appearance variations. Nevertheless, since our metrics primarily capture geometric discrepancies between generated scenes and actual observations, we argue that these discrepancies serve as important indicators of physical execution errors. Moreover, in a video-based policy, the video generator and action decoder jointly constitute the overall policy. Consequently, errors introduced during action decoding can also contribute to discrepancies between predicted and actual physical outcomes.
Our results demonstrate the promise of our approach in identifying physical execution errors manifested as geometric discrepancies. We acknowledge that a more comprehensive assessment of physical consistency, including contact dynamics and object motion, would provide additional evidence. While such an evaluation is beyond the scope of the present work, we consider these aspects valuable directions for future research and will explicitly discuss them in the revised manuscript.
Regarding temporal offsets, each execution cycle begins with an actual observed conditioning frame, from which the corresponding video chunk is generated and its associated action chunk decoded (Appendix B). This design anchors generation and execution to the same initial observation at each cycle, thereby mitigating the accumulation of temporal misalignment across successive cycles.
W2. Related work We thank the reviewer for suggestion. We will add OccScene, ORV, and OmniNWM. These studies demonstrate the effectiveness of incorporating explicit geometric or occupancy representations into scene and video generation. Struct-DPO keeps RGB-only output and uses structure only as a preference signal, so it needs no curated occupancy dataset; it does need environment rollouts, success signals, calibrated cameras, and depth estimation. We will expand the related-work discussion to clarify these methodological differences, including their supervision requirements and the roles of structural representations.
W4. Our experiments address: “Does Struct-DPO improve performance across diverse tasks?” Across 23 tasks, ours achieves an average gain and improves most tasks. While the improvement may appear modest, recently [1] show that SOTA models are often separated by only 1–2%. Thus, our gain supports our claim. Meanwhile, video policy incurs substantial computational costs in experiments, forcing a trade-off between statistical power and task diversity. We chose the latter, as expected of modern video policy, and thus omitted variance. Still, Table below reports standard deviations by treating the Table 1 as six repetitions, which should be interpreted cautiously due to task variation and few repetitions.
Q1. We thank the reviewer for pointing out this inconsistency. The success rates in the real-world experiments were manually recorded by the experimenter, and a recording error led to the incorrect reporting of 65%. The actual result was 32 successes out of 50 trials, corresponding to 64%. We have corrected the reported success rate accordingly.
Q2. We agree with the reviewer that the evaluation settings in Table 7 are inconsistent. However, the methodological observation remains valid: our metric can be replaced by an epipolar criterion within the same pair-construction pipeline. None of the main results in the paper depends on Table 7. We will revise the table and its discussion to make this distinction clear.
Regarding the small baseline difference between Tables 5 and 6, Table 5 uses RoboCasa's automated success evaluation. In contrast, Table 6 relies on manual annotation because RoboCasa does not provide automated metrics for grasp and transport success. We also manually evaluated final task success to maintain consistency across all three milestones. As visually observed task completion may not always agree with the simulator's predefined success conditions, this difference in evaluation criteria may explain the slight discrepancy. We have clarified this point in the revised manuscript.