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- Informativeness
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Paper summary
The paper studies function encoders as a representation of feedback-policy families. It learns shared, vector-valued neural basis functions from expert state-action datasets and represents each policy by a small coefficient vector, typically with eight entries. Once the basis is frozen, the coefficients can be estimated from a demonstration by ridge regression, optimized against a new control objective, or interpolated between policies. The appendix derives coefficient sensitivities and maps coefficient covariance into action and approximate closed-loop trajectory covariance. Experiments cover command-conditioned and motion-conditioned G1 humanoid policies, Go1 locomotion, a planar quadrotor, and LQR, with additional pendulum and HalfCheetah comparisons. The strongest results concern sparse identification within well-covered behavior families, including improvements in Go1 tracking and survival. The paper also reports objective-only synthesis and local interpolation, while documenting failures when behavior coverage is insufficient or interpolated behaviors are distant.
Critical strengths
1 Useful sparse identification with meaningful closed-loop gains
The shared vector-valued basis is a sensible way to couple action dimensions while keeping online adaptation small. It can also represent independently trained experts without aligning their network parameters. G1 coefficient identification takes 0.675 ms on CPU once the 128 context pairs are available, supporting inexpensive inference after observation.
2 Broad evaluation with explicit reporting of limitations
The paper evaluates held-out trajectory prediction and fresh-reset execution, includes disturbed resets, and distinguishes methods with access to sampled demonstrations from methods with access to complete policies. It examines capacity, context size, offline coverage, interpolation, synthesis, and different teacher constructions. The authors also report unfavorable results, including omitted-family failures and unstable interpolation, instead of presenting the linear span as a universally reliable composition mechanism. This makes the study informative and gives useful context for its favorable identification results.
Critical weaknesses
1: Methodological Novelty Is Insufficiently Differentiated From Prior Work
MoS-VLA already represents robot policies as linear combinations of learned vector-valued basis functions with coefficients inferred from demonstrations — the core construction of Eq. 2–4. The distinction that this paper uses coefficients for control behaviors after removing command inputs is relevant but narrow. Directly representing a policy in a learned function space is established prior art, and the paper does not sufficiently isolate what is genuinely novel beyond this design choice.
2: The Key Baseline Is Structurally Incapable of Using Demonstrated Behavior, Making the Comparison Uninformative
The static PULSE-style comparison model largely ignores the variable intended to distinguish different behaviors, meaning different demonstrations do not lead to meaningfully different recovered behaviors. Outperforming this baseline on behavioral accuracy therefore does not establish an advantage over a properly functioning nonlinear alternative. A valid comparison requires first verifying that the baseline actually recovers distinct behaviors from distinct demonstrations, then comparing tracking, task completion, and smoothness under identical conditions — none of which is provided. The paper lacks real-world evaluation.
Questions for authors
Major questions:
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The zombie-walk-to-jog interpolation succeeds in only 22 of 56 trials (39.3%), yet no analysis is provided on when mixing is expected to work or fail. Can the authors provide more behavior pairs and clearer criteria for predicting interpolation reliability?
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The participation rank of 5.58 is derived from the eigenvalue spectrum of an occupancy-weighted metric, but whitening the basis makes any positive-definite metric the identity, yielding rank eight without changing any represented policy. How do the authors establish that this metric measures an intrinsic effective dimension rather than an artifact of basis choice?
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The main Go1 split reuses the same 28 policy functions across offline learning and testing, and the headline G1 unseen-command test covers only two commands and 12 rollouts within the coordinatewise training range. Does the evaluation establish genuine generalization beyond the offline policy support, and can broader out-of-distribution conditions be tested?
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All evaluations are conducted in simulation with no physical robot deployment reported. Can the authors provide real-world results, or at least discuss what sim-to-real gap is expected given the method’s reliance on learned basis functions?
Minor questions: 1 How well does the method work on behaviors absent from training?
Please separate tests of new trajectories from tests of new behaviors. Beyond the existing held-out command and transfer tests, can you evaluate more omitted behavior families on the legged robots and report both tracking accuracy and episode completion across independent training runs?
2 When can two behaviors be mixed successfully?
Can you evaluate more motion pairs, explain why some mixtures fail, and give a practical indication of which pairs are likely to work? The difference between 96.4% and 39.3% success makes the limits of this operation especially relevant.
3 When is searching better than selecting an existing policy?
Please compare search with selecting the best stored coefficient on several new targets. Can you report the total task score, every target component including Go1 height, the number of rollout evaluations, and elapsed search time? This would clarify both the benefit and its cost.
4 Can the nonlinear comparison model use the demonstration effectively?
Can you adjust the static PULSE-style model or add another nonlinear comparison that demonstrably uses the supplied examples to distinguish behaviors? Please evaluate that model with the same data and report task completion, tracking accuracy, and smoothness.
5 How much of a demonstration must be observed before execution?
What happens if the model receives only the first one or two seconds, rather than samples spread across the full trajectory? Please report the observation duration and computation time alongside the resulting execution quality, so the total adaptation time is clear.
6 Which model configuration produced the main comparison results?
Please reconcile the architecture, parameter count, and training-update count in Appendix B.2 and Table 19. Which exact configurations and how many independent training runs were used for Tables 1 and 20?
4 comments
- (W1) Please see our response to Reviewer XFdj, W1. Removing the command input makes the coefficient the task, and the state-feedback form lets one set of coordinates support identification, objective-driven synthesis (Eq. 9), interpolation, and closed-loop uncertainty (Eqs. 12 to 15). MoS-VLA's image-to-action basis has no state dynamics, so it supports neither synthesis nor uncertainty, and no prior function encoder work demonstrates these.
- (W2, Minor 4) The static PULSE-style model is our own construction, built for an information-matched comparison (same 64 state–action pairs, one fixed latent per rollout). Nothing in its structure forces the latent to carry behavior information, so the decoder can ignore it and fit one pooled controller. This collapse is expected, and it is a result, not a miscalibration (App. B.9). The FE avoids it because the policy is linear in the coefficients. The real baseline is the dynamic PULSE model, which follows the original paper. Its latent does carry behavior information, yet it reaches 87.7% success versus 97.7% for the FE, with nearly twice the jerk, despite seeing the reference at every step. We also compare against other baselines including FOMAML, a nonlinear model that uses the demonstration and that the FE outperforms in action error and tracking (Table 1), plus a ridge head, pooled BC, a random subspace, functional PCA, nearest-expert retrieval, a stored-policy simplex, and a parameter subspace (Gaya et al., 2022).
- (Q1, Minor 2) Mixtures carry no intrinsic stability guarantee (as we say in Sec. 4.3). The span is a set of System 0 behaviors, and a higher-level layer would schedule coefficients that keep rollouts stable. Across all 21 pairs of the 7 ProtoMotions behaviors, interior success averages 72.7% (range 21.4% to 100%), and neither endpoint distance nor an endpoint-residual proxy predicts which pairs mix well (Spearman −0.24 and −0.22). We will add these results.
- (Q2) Thank you for identifying this error. The participation rank of M depends on the choice of basis. The invariant quantity is the spectrum of MΣc, the metric-whitened PCA we already report (4 directions, 95.25%), and we will use it instead.
- (Q3) Our claims concern policies within the learned span. Within that scope, we see generalization to held-out behaviors close to the span. On 32 held-out quadrotor tasks, identified policies reach 65.1% success against 64.4% for the analytical teacher (Table 10). On held-out LQR objectives, cost is within 0.002% of the Riccati optimum. On G1, all 56 rollouts on 14 held-out commands survive (Table 5), and held-out action RMSE matches training (0.0438 vs. 0.0427, Table 1).
- (Q4) Real-world experiments are outside the scope of this paper, and we will discuss this in our limitations. Our approach does not address the sim-to-real gap or confer robustness beyond standard simulation-trained policies. The basis can be learned from real trajectories, but deployment would require stronger domain randomization, more data, DAgger, and System 1 behavior synthesis.
- (Minor 1) Our evaluations separate new trajectories from new behaviors (Tables 1, 5, and 10; App. B.5). Table 13 removes each of the four quadrotor families in turn, and on Go1, removing curved walking from training drops its survival from 0.974 to 0.320 (Table 9), as expected. We will add omitted legged families across independent training runs.
- (Minor 3) Retrieval suffices for seen behaviors; search matters for unseen ones. On five held-out Go1 targets, search takes as little as 3.1 s (432 rollouts) with a small loss in performance (mean CMA-ES score −0.349 vs. −0.330 at the full budget), and about 80 s (14,112 rollouts) at the paper's budget. We will report the full ablation, with all error components, rollout counts, and timing.
- (Minor 5) Using only the first 1 or 2 s of a demonstration gives identification accuracy, survival, and tracking comparable to samples spread across the trajectory (see the appendix sample-size sweeps). The linear solve takes 33 to 38 μs, and full identification 0.63 to 0.96 ms. We will add these results.
- (Minor 6) We will fix the mismatch between App. B.2 and Table 19. In Table 1, the G1 joystick and quadrotor rows use a 2$\times$256 SiLU basis over 3 seeds, and Go1 over 4. The ProtoMotions rows (Tables 1 and 20) use a 3$\times$512 SiLU basis (0.678M parameters) trained for 250,000 updates. We will state configurations and seeds in each caption.
Based on the reviewer’s comment, we retrained the static PULSE baseline with to test whether KL regularization contributed to latent collapse. Removing the KL term restored demonstration dependence: swapping demonstration latents increased held-out action RMSE from 0.01582 to 0.25365. In a matched retraining with the original schedule, the error remained approximately 0.01717 with either the correct or swapped latent, indicating that the policy largely ignored the demonstration.
Removing the KL term eliminates the training penalty that pushes the inferred latent distribution toward a standard normal prior. This allows the model to encode behavior differences without paying that regularization cost. The resulting model retains the same static encoder–decoder architecture and provides a stronger nonlinear comparison. From common physical resets, its demonstration latents recovered the intended behavior in 30/35 trials, compared with 5/35 for the matched KL control and 32/35 for FE, according to our diagnostic. Across 700 paired closed-loop trials, FE achieved higher completion (98.0% versus 95.3%) and slightly lower behavior-descriptor error (0.208 versus 0.214). However, the corrected PULSE baseline achieved slightly lower teacher-action RMSE on visited states (0.168 versus 0.169) and a lower action-change rate (5.34 versus 5.55). The corrected comparison therefore shows similar action accuracy and a completion advantage for FE, alongside a modest smoothness advantage for static PULSE. FE’s closed-form coefficient identification remains a separate methodological benefit.
We will revise the PULSE results to distinguish the original KL-regularized model from the model, include the demonstration-swap diagnostic, and report completion, tracking, and smoothness for both. We will also revise the discussion to acknowledge that latent collapse weakened the original baseline and qualify the remaining performance differences.
Thanks to the authors for the corrected PULSE baseline (β=0) and for acknowledging the participation-rank error. Three concerns remain unresolved. 1) The manuscript's novelty over prior work (manuscript Linnes 101–106, page 2; Eq. 2–4, page 3): the core construction \textbf{neural basis functions with least-squares coefficient estimation} is already established in function encoders (Ingebrand et al., ICML 2025) and applied to robot policies in MoS-VLA; synthesis, interpolation, and uncertainty follow naturally from that same linear structure, and the response does not isolate a genuinely new algorithmic contribution beyond this. 2) is corrected PULSE comparison (authors comment on 16 Nov): the β=0 baseline is now a properly functioning nonlinear model, yet the FE’s advantage is only a 2.7% completion gap (98.0% vs 95.3%), matched action accuracy (0.168 vs 0.169 RMSE), and a smoothness disadvantage (action-change rate 5.55 vs 5.34), confirming the original comparison was uninformative and that the advantage over a working nonlinear baseline is modest. 3) Interpolation reliability (manuscript Page 8, Sections 4.3; authors’ Q1 response): the 39.3% zombie-walk-to-jog success remains unexplained; however, the authors confirm neither proxy predicts which pairs mix well (Spearman −0.24 and −0.22), and real-world evaluation (I cannot see any value for real-world validation) was explicitly declined. I still maintain my rating.
We thank the reviewer for their feedback. We maintain that the contribution does not follow automatically from the shared linear formulation. A natural operation does not automatically establish a capability, and none of the demonstrated capabilities in our work are investigated in prior art. Our central contribution is demonstrating that one learned feedback-policy basis supports sparse identification from expert demonstrations, runtime synthesis of behaviors from task objectives, and interpolation, together with our analysis of policy sensitivity and identification uncertainty. These operations reuse the same representation without retraining the basis. The prior work establishes the underlying construction, but does not investigate this.
The corrected PULSE results show that a nonlinear latent model can achieve comparable performance on this task. This narrows the performance claim for that comparison, but our approach remains the only one that supports the combined capabilities we investigate.