1. Expert selection and multi-expert merging are not sufficiently disentangled.
This is my primary concern. Table 14 shows that multiple experts are merged in only 1.44% of RoboCasa SFT episodes, 1.22% of RoboCasa SFT+RL episodes, and 6.60% of LIBERO episodes. According to Equation (2), the remaining episodes execute exactly one selected expert. If this lose the sense of your method?
The LIBERO comparison is informative: Top-1 selection with the same scorer achieves 73.2%, whereas adaptive merging achieves 75.4%. However, corresponding matched Top-1 closed-loop results are missing for the main RoboCasa SFT, RL, and real-world experiments. Consequently, the contributions of independent specialization, expert identification, and actual multi-expert merging remain insufficiently separated.
In particular, the paper does not report the performance of the true-task-ID-selected expert on the subset where merging is triggered. Merging might exploit complementary capabilities, or it might primarily compensate for errors made by the proposed scorer. These explanations imply different contributions and should be distinguished experimentally.
2. The co-training comparisons do not adequately establish the practical advantage of the proposed deployment strategy.
The LIBERO comparison omits representative strong fine-tuning baselines. OpenVLA-OFT reports 94.5% on LIBERO-Long, and its single policy jointly trained across all four suites achieves 95.3% on the Long suite. The official openpi implementation reports 92.4% for fine-tuned π0.5. In comparison, this paper reports 72.4% for co-trained GR00T, 80.8% for individual experts, and 75.4% for PolicyWeave.
There is also insufficient information about the simulated co-training SFT budgets. Each expert receives 10,000 training steps, totaling 180,000 steps for RoboCasa and 100,000 for LIBERO, while the co-training baselines use official checkpoints without a sufficiently explicit account of their training budgets and adaptation configurations. Matching the demonstration fraction does not establish computational comparability.
These issues weaken the argument for independently training and consolidating experts over a well-optimized joint policy. They do not invalidate the interface result, but the practical benefit of maintaining an expert bank remains insufficiently demonstrated.
3. The action-interface experiments do not sufficiently isolate the contributions of individual components.
The principal comparison simultaneously changes whether normalization, the encoder, and the decoder are task-specific. Table 3 replaces components after experts have already been trained. This demonstrates sensitivity to incompatible interfaces, but it does not isolate the contribution of each constraint during training.
A controlled training-time ablation—such as shared versus task-specific normalization crossed with frozen versus trainable input-output projectors—would clarify which components drive the improvement. Both individual and merged performance should be reported to determine whether freezing the complete interface is necessary and whether it imposes an adaptation cost.
4. Generality is supported only within one backbone and task-covered expert banks.
All PolicyWeave experiments use GR00T N1.5. Including π0.5 as a co-training baseline or reproducing MergeVLA on its own backbone does not validate PolicyWeave on another architecture. The benefits of freezing the action interface and the usefulness of key-response scoring may depend on the backbone and its pretraining procedure.
The task scope is also limited. RoboCasa evaluation covers 18 Atomic-Seen tasks, each evaluated over 50 episodes. These tasks already appear in pretraining. Although target kitchens differ from pretraining kitchens, target adaptation itself uses target-domain demonstrations. The paper does not evaluate the Composite-Seen or Composite-Unseen task groups. Official RoboCasa dataset definitions.
5. Scalability is only partially characterized.
At the beginning of each episode, the method still scores every expert. A shared base pass and low-rank computations reduce the cost, but scoring and adapter storage grow linearly with the number of experts. Sparse execution does not eliminate the full-bank search.
Table 18 provides useful measurements, but only up to 18 experts, using 250 recorded contexts from five tasks. Latency is measured with a batch size of five and the entire model and expert bank already resident on the GPU. This does not establish single-request end-to-end latency or selection reliability for substantially larger banks.
The evaluation should distinguish computational scaling from interference caused by additional candidates. Adding increasingly similar and unrelated experts while measuring closed-loop success, routing accuracy, selected-set size, latency, and memory would be informative. Because the implementation applies updates in low-rank form, the paper should also distinguish mathematical equivalence to merged weights from empirically demonstrated inference overhead.
Dear Reviewer yDMx,
With the discussion period nearing its end, we would like to follow up to see if our response has resolved your questions. We would be glad to provide any further clarification if needed.
Best regards,
The Authors