1. The distinctive contribution of the method and its underlying mechanism are not yet sufficiently substantiated.
The parameterization of skill goals, the per-joint blending scheme, and the use of a frozen primitive library are all inherited from SkillBlender [1]. CooHOI [2] has already enabled multiple simulated humanoid characters to learn collaborative manipulation by exploiting object dynamics through a shared policy and MAPPO, although it fine-tunes a motion-prior-based single-agent policy rather than blending frozen RL-pretrained primitives. In addition, MAPush [3] and decPLM [4] are relevant precedents for quadruped teams, and neither is discussed in the manuscript. Both train a shared decentralized policy with MAPPO on top of a frozen locomotion controller to perform collaborative manipulation.
The existing experiments do not sufficiently isolate this contribution. The most evident comparative advantage appears on Move, but this task uses only a single primitive, Walking (Table 2). In this case, every per-joint blending weight is identically 1, so the task does not test non-trivial skill blending. The skill-removal ablation (Fig. 5) shows that the removed primitives (Squatting for Carry, Walking for Push) are important for learning performance. However, it does not establish whether per-joint blending outperforms other hierarchical methods with comparable motor capabilities.
The permutation theorem likewise does not explain the source of the improvement. For a shared local policy, consistently permuting observations, actions, stored advantages, and old-policy log-probabilities merely rearranges the same set of actor loss terms. Under consistent mean reduction and normalization, the averaged actor optimization objective remains unchanged. Algorithm 1 computes advantages before augmentation and applies augmentation within each sampled minibatch, so this issue is directly relevant to the training procedure described in the manuscript. Section 4.3 explicitly trains the centralized critic on original and permuted states with the same return targets, which may improve subsequent advantage estimation; details of the optimization procedure may also affect training. However, Theorem 2 relies on true value and advantage functions and does not establish these practical mechanisms. Consequently, the ablation between the full method and the no-augmentation variant cannot yet determine where the gains originate. The manuscript should also explicitly discuss its relationship to permutation-invariant critic methods such as PIC [5].
2. The current comparative experiments are insufficient to establish a robust advantage over related methods.
Section 5.2 reports only two independent training runs and evaluates the best learned policy with 50 rollouts, but does not define the meaning of “±” or specify the checkpoint selection rule. The Carry success rates correspond to 50/50, 49/50, and 48/50 successful episodes, respectively, while Push corresponds to 43/50, 42/50, and 39/50. These small differences, together with the practice of selecting the best policy for evaluation, are insufficient to demonstrate a reliable advantage across independent training runs. The large gap between the full method and the no-augmentation variant on Carry in Table 4 is noteworthy, but repeated experiments and component-level attribution analyses are particularly needed.
The comparison with TeamHOI [6] is also affected by how the baseline was adapted. For Carry and Push, Appendix F.4 makes two changes. First, it removes explicit teammate information to match MASkillBlender’s observations. Second, it replaces the original distance-dependent switching between Full and Masked AMP with a fixed per-task choice, which the appendix justifies by near-object initialization and empirical training performance. Teammate-conditioned inputs and interaction-dependent masking are core components of the original method, so these changes limit what the Carry and Push comparisons can show about TeamHOI’s capabilities.
On Move, neither change applies: closest-teammate information is retained, and there is no object interaction to mask. Here the policy learns to face the target but does not reach it. This failure more likely reflects other adaptation choices, such as retargeting to H1, the selection of locomotion references, or the equal weighting of task and AMP rewards. Unless the adapted baseline is validated, this result should not be taken as evidence about reference-based methods in general.
In addition, the manuscript does not report the success rate for G1, and the statistical aggregation of the MuJoCo results requires clarification.
[1] Kuang et al. SkillBlender: Towards Versatile Humanoid Whole-Body Loco-Manipulation via Skill Blending. arXiv:2506.09366, 2025.
[2] Gao et al. CooHOI: Learning Cooperative Human-Object Interaction with Manipulated Object Dynamics. arXiv:2406.14558, 2024.
[3] Feng et al. Learning Multi-Agent Loco-Manipulation for Long-Horizon Quadrupedal Pushing. arXiv:2411.07104, 2024.
[4] Pandit, Shrestha, and Fern. Multi-Quadruped Cooperative Object Transport: Learning Decentralized Pinch-Lift-Move. arXiv:2509.14342, 2025.
[5] Liu, Yeh, and Schwing. PIC: Permutation Invariant Critic for Multi-Agent Deep Reinforcement Learning. Proceedings of the Conference on Robot Learning, PMLR 100:590–602, 2020.
[6] Lionar and Lee. TeamHOI: Learning a Unified Policy for Cooperative Human-Object Interactions with Any Team Size. CVPR, 2026.
Thank you for the detailed responses and the additional analyses and experiments. The rebuttal substantially addresses the main concern in my original review about the relationship between the permutation argument and the implemented learning procedure, and it strengthens the empirical evidence for the system.