The temporal stress behind the main comparison is generated by author-designed service traces, so the external validity of the gains remains open. In S1, modality availability follows a Markov process with drop probability 0.30 and persistence 0.80, delays are drawn uniformly from 0 to 8 rounds, and CrisisMMD receives additional affine feature drift (Appendix E.1). The delay-modality coupling ρ_τM that the study identifies as the mechanism is thus a design parameter rather than a measured property of an asynchronous deployment. The conclusions about real-world nonstationarity are correspondingly tentative.
The quantities that connect the theory to the empirical improvements are not assessed on real data. The conditions of the utility analysis involve the true drift, the use-time displacement, and the local coordinate mismatch, none of which is observable without latent ground truth, and the corresponding check in Fig. 4(d) is confined to the CREMA-D-calibrated environment. The identification bound likewise contains the state-estimation error and a residual confounding term as non-vanishing floors, so part of the guarantee is conditional on the accuracy of the smoother from which the transition is fitted. The orthogonal gauge assumption and the representation error term also appear unquantified for the heterogeneous encoders used in the experiments.
The protocol leaves details unspecified that are needed to interpret the margins. Although Appendix E.1 states that the backbone-parameter protocol is fixed across matched comparisons, the paper does not say whether the reported FedLWM configuration includes the parameter channel: Table 4 separates a world-channel variant (0.72 KiB per regular round) from a world-plus-parameter variant (7.63 MiB plus 0.72 KiB). The labels E-P, E-G1, E-G1′, and E-G2 are defined only in captions, and ACI is never expanded. Which configuration underlies the reported comparisons is therefore not fully clear.
The main comparison tables report point estimates without dispersion or significance assessment. Table 1 states that results are averaged over five seeds but gives single numbers, and Table 2 likewise omits dispersion for its accuracy columns. The absence of uncertainty makes it difficult to judge whether margins such as the 1.07-point S1 E-P lead over FedAsync on MELD (35.97 versus 34.90) are reliable. The extent of the advantage over the strongest baselines therefore remains uncertain.
Theorem 1 appears to restate an information-loss argument rather than a property of federated aggregation. Its proof exhibits two admissible states with equal chart-wise mean and raw second moment that diverge after a weight-mixing transition, so the floor follows for any map of the summary. Because the empirical baselines do not predict dynamics from aggregate moment summaries, the result mainly accounts for the B-Mom ablation, and the "relocation is forced" framing reads as stronger than the construction establishes. The statement is correct, but its scope relative to moment-closure arguments is narrower than claimed.
Paper Formatting and Clarity Concerns
E-P, E-G1, E-G1′, and E-G2 are not expanded at first use, and ACI in Table 5 and Appendix E.2 is used without its full form, so readers may need to infer the metrics from context.
The figures are information-dense at page scale: Figure 4 packs four panels with small axis labels, and the insets in Fig. 5 are difficult to inspect at normal zoom.
The caption of Table 6 states that E-G1′ applies dropout to "the S0 shared model", while Table 1 and Table 2 do not specify which model this metric uses, so comparisons of the missing-modality column across tables may be ambiguous.
Thanks for the author's detailed rebuttal. My questions and concerns have been addressed.
I decide to maintain my score, as it reflects my overall assessment of this work.