- Rating
- 1
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
This paper proposes OvaDiP, an analysis framework for structured diffusion paths in which different orthogonal subspaces of the data follow different noise schedules. In the EDM setting, each subspace (in practice, one of three DCT frequency bands) receives its own noise level , and the deformation operator is split into a rank-weighted common component , called common retiming, and a trace-free residual , called centered structural redistribution. The paper is motivated by the observation that its structured paths give lower mean FID than the scalar reference on CIFAR-10, CIFAR-100, and AFHQv2, but higher mean FID on FFHQ. The analysis then proceeds in three steps. First, a 2×2 factorial design on CIFAR-100 (Reference, common retiming only, centered redistribution only, and Full) evaluated at NFE7, NFE15, and NFE31 shows that common retiming is the only resolved effect at NFE7, whereas centered redistribution and the Full path are resolved at NFE15 and NFE31, and the factorial interaction is not resolved at any budget. Second, on AFHQv2 and FFHQ, every trained model is evaluated under every sampling path in a 4×4 grid, which decomposes the Full-versus-Reference contrast into a trained-state term and a path-return term, and the factorial interaction into , with exact algebraic closure. Using this decomposition, the authors report that small final FID differences can conceal substantially larger, opposing trained-state and sampling-path contributions. Third, by tracking , , and across aligned CIFAR-100 checkpoints, the paper reports that the sign of the interaction can appear stable while its training–sampling attribution continues to change late in training, and a separate late-change test on another seed finds a change in that exceeds the three-block Monte-Carlo variation. The appendix additionally applies the construction to a rank-matched Haar projector and to a small NAVSIM-mini trajectory-generation setting. The authors state that the attribution terms are conditional on the chosen common sampler and that the findings are specific to the finite systems studied.
Critical strengths
The paper raises a legitimate methodological question. Changing the diffusion path changes both what the denoiser learns during training and the trajectory followed during sampling, so an end-to-end FID difference conflates the two stages. Prior work on structured or anisotropic schedules (e.g., Scimeca et al., 2025; Liu et al., 2026) mostly reports only end-to-end metrics, and the paper's central message, that a final generation metric alone can obscure how an observed effect arises, points in a useful direction. The paper is also careful about the scope of its claims. The authors state explicitly that the attribution terms are "common-sampler-conditioned rather than intrinsic training or sampling effects" (Section 4.1), that the closure checks do not test whether the identity is statistically true (Appendix B.7), that the Monte-Carlo radii are not population confidence intervals (Appendix D.6), and that the findings should not be interpreted as universal properties of structured diffusion paths (Section 6). As discussed under Weaknesses, however, the current execution does not yet support this message.
Critical weaknesses
1. The phenomenon the paper sets out to explain, and the effects it analyzes, are not statistically resolved
The paper is motivated by a cross-dataset "puzzle": its structured path lowers FID on CIFAR-10, CIFAR-100, and AFHQv2 but raises it on FFHQ. Yet a paired test of Full versus Reference across training seeds gives 95% confidence intervals of [−0.64, +0.17] on AFHQv2 and [−0.99, +1.29] on FFHQ, and one of the three FFHQ seeds goes in the opposite direction. The mean differences (−0.23 and +0.15 FID) are on the same order as the across-seed standard deviations (0.15 to 0.52), and they are measured with three seeds, 4,096 samples per cell, and models trained for only 5 Mimg. The quantities interpreted later are similarly unresolved: the CIFAR-100 factorial interaction has confidence intervals containing zero at all three budgets, and its per-seed values on AFHQv2 (−0.78, +0.39, −0.78) and FFHQ (−0.12, +0.32, −0.04) do not even agree in sign. The training-dynamics claims rest on two fresh seeds and a single seed for the late-change test, with uncertainty estimated only from generation blocks, so training-time variability is not captured. All models are also severely undertrained (5 to 10 Mimg versus about 200 Mimg in standard EDM training; the CIFAR-10 baseline FID is 7.02 versus about 2 in EDM). This weakness is consequential because the paper has no established effect to explain: the motivating sign difference and most of the interpreted quantities lie within the measurement resolution, and it is unclear whether any of them would persist under standard training.
2. The training–sampling attribution measures out-of-distribution mismatch penalties, not training and sampling contributions
The attribution relies on cross-evaluations in which a model trained on one path is sampled with another, and these evaluations are far out of distribution: same-group pairings give FID of about 10 to 14, whereas cross-group pairings give 20.7 to 36.8 (Tables 13 and 14). This is expected, since the network's noise embedding receives only the rank-weighted mean of the per-band log noise levels (Appendix B.5), so the R and G models never see unequal noise across bands during training. Expanding Eq. 67 shows that the symmetric "sampling contribution" is exactly half the asymmetry between the two mismatch penalties, with and , while . The headline finding, that small FID differences conceal large opposing contributions, therefore follows whenever ; on FFHQ, for instance, the two penalties are about 22 to 23 and 8 to 9 FID, which yields terms of about ±7 against a total difference below 0.6. The two orderings that the paper averages as a "robustness check" give training contributions of opposite sign in all six runs (+7.7 to +16.2 versus −16.9 to −22.9; Table 19). Moreover, the attribution shows the same qualitative pattern on AFHQv2 (improved) and FFHQ (degraded), so it does not explain the cross-dataset difference it was introduced to explain. This weakness is consequential because the attribution is the paper's main contribution: the path parameterization belongs to the same class as existing per-band schedules (Scimeca et al., 2025; Liu et al., 2026; Gerdes et al., 2024), and the decomposition tools correspond to standard Oaxaca–Blinder, Shapley, and factorial analyses. Once the attribution is read as a measure of robustness to unfamiliar sampling paths, the central finding loses its intended interpretation, and the paper's motivating question remains unanswered.
Questions for authors
Clarification requests
The answers to the following questions could materially change my assessment.
Q1. Is the motivating cross-dataset sign difference statistically supported? The paired 95% confidence intervals for Full minus Reference are [−0.64, +0.17] on AFHQv2 and [−0.99, +1.29] on FFHQ, and one of the three FFHQ seeds favors the structured path. On what basis is the FFHQ result treated as a degradation that requires explanation? Do additional seeds or 50,000-sample FID evaluations exist for AFHQv2 and FFHQ, and do they resolve the sign of the effect? This question bears on Critical Weakness 1.
Q2. How should the T/S terms be interpreted, given that the cross-evaluations are out of distribution? Expanding Eq. 67 gives , where and . Do you agree with this identity, and if so, what distinguishes the reported sampling-path term from the asymmetry between two mismatch penalties? Beyond the rank-weighted mean in the noise embedding and the per-band preconditioning (Appendix B.5), does the network receive any information about the per-band noise levels, and were the R and G models ever exposed to unequal per-band noise during training? Since cross-group evaluations reach FID 20.7 to 36.8 while same-group evaluations stay around 10 to 14, why should these cells be treated as valid counterfactuals for the trained models? This question bears on Critical Weakness 2.
Q3. How robust is the attribution to the ordering and to the choice of common sampler? The two ordered decompositions that are averaged in Eq. 13 give training contributions of opposite sign in all six runs (Table 19). What makes their average a meaningful attribution rather than a small residual between two large and conflicting estimates? In addition, for AFHQv2 seed 3, is +1.98 under both the R and G samplers but −1.55 and −1.58 under the C and F samplers (Table 15). Why is Y = F the appropriate main choice, and which conclusions in Section 4.2 still hold under Y = R?
Q4. Which part of the analysis explains the cross-dataset difference? Section 4 reports the same qualitative cancellation pattern on AFHQv2, where the structured path improves FID, and on FFHQ, where it degrades FID. Is the difference in magnitude between the two datasets intended as the explanation, and if so, how does it account for the difference in sign? If the attribution is not meant to explain this difference, how does the paper answer the question posed in the introduction?
Q5. Are the late-training changes distinguishable from training variability? The uncertainty in Section 5 is estimated only from three generation blocks, which captures sampling randomness but not checkpoint-to-checkpoint training variability. Is there any estimate of training variability, for example from adjacent checkpoints or additional seeds, showing that the jump for seed 23 (from −1.52 to +0.99 between 90% and 100% of training) and the change in for seed 24 exceed it? Relatedly, do you expect these dynamics to persist under a training budget closer to standard EDM training, given that the current runs use only 5 to 10 Mimg?
Response to Reviewer YFAt (Q1–Q5)
Q1 — Dataset-level FID differences. The opposite AFHQv2 and FFHQ mean directions are not statistically established. Table 1 now reports descriptive differences and training-seed SDs; Section 2 adds paired 95% intervals. At NFE63, Full−Reference is −0.235 [−0.637,+0.168] on AFHQv2 and +0.146 [−0.994,+1.285] on FFHQ (three training seeds each). Both intervals include zero. CIFAR-100 at NFE31 gives −0.969 [−1.344,−0.594] across five seeds. We no longer treat the AFHQv2/FFHQ means as a confirmed cross-dataset reversal.
Q2 — Meaning of the T/S terms and mismatched evaluations. We agree with the algebraic observation. Writing JX∣Y for the FID of trained state X under sampler Y, let mR=JR∣F−JR∣R and mF=JF∣R−JF∣F. The symmetric path-return term is exactly Ssym=(mR−mF)/2. Large opposing T/S terms can therefore reflect directional model–sampler mismatch, rather than separately identifiable causal stage effects. R is trained with a common scalar noise schedule, whereas C uses subspace-specific noise schedules. With
structure_condition=none, the denoiser's noise embedding uses a rank-weighted mean log-noise rather than an explicit per-band noise vector; input/skip/output preconditioning remains bandwise. Off-diagonal evaluations, sometimes with substantially worse FID than matched pairs, are diagnostic compatibility probes, not in-distribution counterfactuals.Q3 — Choice of common sampler. We report Y=F because it matches the Full-trained state, not because F is neutral. All four R/G/C/F evaluators are now reported. The matched interaction I is fixed, and I=QY+PY holds for every Y, but the terms are evaluator-dependent. In AFHQv2 seed 3, choosing R instead of F changes QY from −1.582 to +1.979, reversing its sign. Thus conclusions about the attribution terms must name the sampler.
Q4 — What the cross-evaluations add. Under an additive model–sampler response JX∣Y=aX+bY, the factorial trained-state contrast QY would not depend on Y. The observed within-seed ranges are 0.204–3.561 FID on AFHQv2 and 0.367–0.693 on FFHQ; all three FFHQ seeds retain their signs. This measured non-additivity is not implied by the accounting identity. It may be mismatch-driven and does not explain FFHQ's matched FID direction.
Q5 — Late-training evidence and its limits. Our claim concerns the fixed 10-Mimg CIFAR-100 budget, not convergence under a longer EDM schedule. Seed 23 shows Q and I sign reversals between 90% and 100%, with endpoint signs resolved across disjoint generation blocks. In the independently trained, prospectively frozen seed-24 test, block A selected the 80–90% interval from two prespecified candidates; blocks B/C were held out of that choice. The block-averaged change is ΔQ=+1.9022, above the empirical generation-block variation radius of 0.3629; ΔI=+1.4417 also changes. Seed 22 has a retrospective I-sign certificate from 70%, but no earlier Q/P-relation certificate; a missing certificate is not itself evidence of movement. The generation blocks measure finite-sample variability within a training run, not training-seed uncertainty. We cannot infer what happens under a longer training budget.