W1: The experiments do not adequately isolate the choice of transport operator or the contribution of progressive rank growth. The transport controls (Tables 5 and 12, Fig. 16) copy historical coefficients rather than mapping them into the new basis, and the task suites never compare Procrustes with least-squares transport under the same basis and rank trajectory. Appendix B.3 derives the reconstruction trade-off between the two analytically, but the only numerical comparison is the synthetic example in Table 6. The residual diagnostics defined in Appendix F also do not appear to be reported for real experts. For rank, Appendix H shows that capacity matters on CLIP: at the 1/t scale, fixed rank 128 exceeds fixed rank 64 by 2.3 points (Table 13). However, this is a single run (seed 11, O1), and beyond a 0.1–0.2-point difference between the main schedule and constant rank 256, it does not establish a benefit of progressive growth over a constant cap. On CLIP, with rank-8 experts, the requested caps of 64, 128, and 256 at 8, 14, and 20 arrivals meet or exceed the available directions at each milestone, so the cap does not truncate at those points (the paper does not say whether the energy rule also truncates there; see W4). On Scene32, the resource calibration ends at ranks of only 16–18 after 32 arrivals, so caps of 64 and 256 yield identical states (Sec. 4.4). Procrustes transport and progressive capacity are central to the paper’s framing, so it remains unclear how much of the main-suite performance is attributable to each (see Q2, Q3).
W2: The empirical gains are modest in several settings, and their uncertainty is not quantified. On CLIP-20, PLEAT’s cross-backbone average of 59.9 is only 0.3 points above the pretrained reference of 59.6, and on ViT-B/16 it matches the reference (60.3 vs. 60.33, Table 4). At 14 tasks, PLEAT falls below the pretrained reference on all three backbones, as do all compared methods, although the reference uses canonical-order prefixes while the merging methods average three arrival orders. Margins over the strongest reported baselines are 0.9 points on LLaVA (TIES, normalized mean, Table 2), 0.5 on DriveLM (OPCM, Table 3), and 0.8 on CLIP (K-Merge, Table 4). In Fig. 4, which appears to report LLaVA-8, OPCM is within 0.1 points of PLEAT on the expert-relative score. The paper reports no confidence intervals or paired significance tests for these comparisons. Because all methods share the same experts within a seed, the relevant quantity is the paired margin, yet baseline results are not reported per seed. On CLIP, the 0.8-point margin is smaller than PLEAT’s own across-seed range of 59.2–60.4 (Table 9), which does not by itself establish significance but means the margin cannot be assessed without paired results. Finally, in the single-run seed-11, O1 analysis, PLEAT’s fixed early-task cohort accuracy falls to 50.0 at 20 tasks, below NUFILT’s 55.6 (Table 12), although its backward transfer (+2.9) is the highest of the four methods, so the aggregate endpoint does not fully characterize retention. Since the abstract claims that PLEAT outperforms a range of existing merging methods, small margins without uncertainty estimates limit how strongly this can be concluded (see Q6).
W3: The incoming alignment introduces an uncontrolled rescaling of each expert. Proc(At,Qt) is not invariant to general factor reparameterizations (BtGt,Gt−1At) of Eq. 2 (it is invariant to orthogonal Gt, but not to rescalings or other invertible Gt), so the magnitude of an expert’s contribution depends on how its scale is split between At and Bt, not on its update BtAt alone. For example, absorbing the loader multiplier into At rather than Bt (Sec. 3.1) would change each expert’s contribution by that factor. In the reported configurations α/r=2 for every expert (Appendix C), so if the loader multiplier is α/r, this particular change would be a global scale, but the same argument applies to any per-expert split of scale between At and Bt. Eq. 21 further shows that the singular values of AtQt⊤ are replaced by 1, so incoming reconstruction is inexact even when At lies in the span of Qt, unless its rows are orthonormal. The paper notes the scaling term (Appendix B.5) but does not quantify it for real experts. The crossed controls in Appendix F (Eq. 22) toggle Procrustes against a coordinate-copy map E, so they test whether alignment helps, not how much of that effect is due to the rescaling. Appendix C also states that the exact paired mean has no tuned parameter, whereas PLEAT’s configuration search includes a scale range (see W4), so a difference in effective scale could contribute to the gap as well. No experiment separates the rescaling from the geometric alignment, so part of the reported gains over baselines that apply no such rescaling (e.g., the paired mean) may come from it (see Q1).
W4: Several baseline rows and reported settings are inconsistent across tables, which makes some comparisons hard to interpret:
• “Paired mean” matches “Independent factor mean” (Table 5) on LLaVA and CLIP but not on DriveLM or Scene32, although Eq. 1 shows these are different operators. The “Uniform” row in Table 2 matches neither (Q4).
• OPCM appears in Fig. 4 but is absent from Table 2 (Q5).
• Table 4’s ViT-B/32 20-task values appear to match a single seed and order rather than the stated three-seed, three-order average (Q5).
• The export scale is listed as fixed at 1/t (Table 10), but Appendix C describes a search over a scale range of [0.1,1.0]; it is unclear whether this range is absolute or relative to 1/t.
• CLIP’s rank rule is described as a schedule (Sec. 3.3) but listed with an energy threshold and a single cap (Table 10).
Because these concern the main comparisons and settings, they weaken confidence in the headline results until clarified.