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Under review as a conference paper at ICLR 2027

OvaDiP: Controlling Structured Diffusion Paths, Separating Training and Sampling Contributions, and Tracking Their Dynamics

Abstract

We introduce Operator-Valued Diffusion Paths (OvaDiP), a controlled analysis framework for structured diffusion paths whose final effects can vary across datasets. OvaDiP represents a structured path as an operator-valued deformation of a scalar reference and canonically separates its variation into common retiming and centered structural redistribution. Controlled factorial interventions along these two coordinates show that their effects depend on the sampling budget. We then use common-sampler cross-evaluation to separate the contributions associated with the trained model and the sampling path. Across AFHQv2 and FFHQ, small final Fréchet Inception Distance (FID) differences can conceal substantially larger opposing contributions from these two stages. Finally, we extend the same attribution across training and find that the factorial interaction can appear stable while the balance between training and sampling continues to evolve late in training. Together, these results show that a final generation metric alone can obscure how the observed effect of a structured diffusion path arises. OvaDiP provides a controlled framework for relating path interventions to training–sampling attribution and its evolution during training. Our implementation and evaluation code are available at https://anonymous.4open.science/r/ovadip.

Primary area:
generative models
Keywords:
diffusion models, generative modeling, structured diffusion paths, noise schedules, diffusion sampling

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_YFAtOpenReview ↗
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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 σk(u)=σ(u)exp⁡(−λDk(u))\sigma_k(u) = \sigma(u)\exp(-\lambda D_k(u)), and the deformation operator D(u)D(u) is split into a rank-weighted common component g(u)Ig(u)I, called common retiming, and a trace-free residual D∘(u)D^\circ(u), 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 I=Q+PI = Q + P, 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 II, QQ, and PP 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 QQ 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, SF−Rsym=12(MR→F−MF→R)S^{sym}_{F-R} = \frac{1}{2}(M_{R\to F} - M_{F\to R}) with MF→R=JF∣R−JF∣FM_{F\to R} = J_{F|R} - J_{F|F} and MR→F=JR∣F−JR∣RM_{R\to F} = J_{R|F} - J_{R|R}, while TF−Rsym=ΔJF−R−SF−RsymT^{sym}_{F-R} = \Delta J_{F-R} - S^{sym}_{F-R}. The headline finding, that small FID differences conceal large opposing contributions, therefore follows whenever ∣Ssym∣>2∣ΔJ∣|S^{\mathrm{sym}}| > 2|\Delta J|; 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 SF−Rsym=12(MR→F−MF→R)S^{sym}_{F-R} = \frac{1}{2}(M_{R\to F} - M_{F\to R}), where MF→R=JF∣R−JF∣FM_{F\to R} = J_{F|R} - J_{F|F} and MR→F=JR∣F−JR∣RM_{R\to F} = J_{R|F} - J_{R|R}. 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, QQ 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 QQ 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?

1 comment
AuthorsOpenReview ↗

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∣YJ_{X\mid Y} for the FID of trained state XX under sampler YY, let mR=JR∣F−JR∣Rm_R=J_{R\mid F}-J_{R\mid R} and mF=JF∣R−JF∣Fm_F=J_{F\mid R}-J_{F\mid F}. The symmetric path-return term is exactly Ssym=(mR−mF)/2S_{\mathrm{sym}}=(m_R-m_F)/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=FY=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 II is fixed, and I=QY+PYI=Q_Y+P_Y holds for every YY, but the terms are evaluator-dependent. In AFHQv2 seed 3, choosing R instead of F changes QYQ_Y 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+bYJ_{X\mid Y}=a_X+b_Y, the factorial trained-state contrast QYQ_Y would not depend on YY. 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\overline{\Delta Q}=+1.9022, above the empirical generation-block variation radius of 0.3629; ΔI‾=+1.4417\overline{\Delta I}=+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.

Reviewer_rMxzOpenReview ↗
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Informativeness
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Paper summary

Structured diffusion, wherein the noise schedule can be different across different subspaces/frequencies, has been shown to sometimes improve generation quality as measured by FID.

The authors begin by reparameterizing the structured noise schedule as σ(u)e−λ∗D(u)\sigma(u) e^{-\lambda*D(u)} with D(u)=0D(u) = 0 recovering the original isotropic noise schedule. They then provide a motivating experiment that shows the FID improvement of structured diffusion is not necessarily consistent across different datasets.

In order to help explain this they propose breaking DD down into a component that is shared across subspaces and a centered structural redistribution term. They then distinguish between FID values computed with each of these two components applied individually, and then together, and also reference FID with the scalar noise schedule. Afterwards they report these FID values for CIFAR-100 across different sampling budgets (NFEs). The results show that the two components don't additively affect the FID as represented by the interaction II that measures how much of the combined effect can be accounted for by adding up the effects of each component. (I=0I = 0 means the effects are additive)

Next they separate the FID change, into two components: change induced by the differing training scheme QQ (structured vs non-structured) and differing sampling scheme PP (structured vs non-structured). They show that QQ and PP can have different signs.

Finally they empirically look at the trends of QQ and PP during training and claim that a consistent II can mask the changes in attributions QQ and PP during different stages of training.

Critical strengths

1- The motivating example of structured diffusion not always leading to higher quality generations is interesting and worth studying.

2- The decomposition of the operator valued structure into a component that is shared across subspaces and a centered structural redistribution term is an interesting idea.

Critical weaknesses

1- My main issue with the paper is the following: They begin with a motivating example that it is unclear why structured diffusion does not necessarily lead to improved FID. But that having read the paper carefully, the results and claims presented (to my understanding) do not give any insight on the motivating question.

The decomposition of the structured noise schedule into a common component and a zero-trace redistribution is intriguing, but then the empirical results present the FID changes induced by these components and leave it at that without trying to provide any intuition or understanding of why these values are different or what these differences mean/represent.

This trend of presenting a lot of numerical results onto the reader with very little explanation as to their significance or how the reader should interpret them is a consistent weakness throughout the paper.

2- The entire training-sampling attribution section is very vaguely motivated and its significance is unclear. It seems arbitrary to decompose the change in FID into change induced by modifying training scheme while keeping sampling the same and vice versa. I say this because it makes sense to use the same structured schedule in sampling as in training so why would we decompose in this way and what insight does it give us? Similarly, it is pointed out in section 5 that QQ and PP can change during training while II stays more or less the same without any explanation as to why this is a relevant observation.

3- The presentation of the paper is severely lacking throughout. Setting aside the lack of proper motivations and explanations as mentioned in the previous two weaknesses, the writing is difficult to follow. There are many paragraphs talking about the numerical results without making any meaningful or interpretable points. Many parts of the paper are dense in new definitions while also being sparse in technical content or intuition. Even the abstract is very difficult to parse without reading the whole paper.

4- The experimental results seem limited in scope to the detriment of the claims made. For example in the motivation experiments In Table 1, we have four datasets total, and in 3 of those 4, structured diffusion leads to better FID, and in the single one where it doesn't (FFHQ) the error bars are large enough that it isn't clear whether or not there is an improvement. Looking at these I would be hesitant to claim structured diffusion isn't always better. More datasets could be helpful in this regard to paint a clearer picture.

Questions for authors

1- The paper is motivated by asking why structured diffusion does not necessarily improve FID. Can the authors state concisely what their answer is, and point to the specific results that support it?

2- What does each component, the common component and the zero-trace redistribution, represent intuitively, and why do they produce different FID changes? Is there a mechanistic explanation, ideally backed by qualitative or per-frequency evidence, and does it lead to any practical recommendation?

3- Since a structured schedule would naturally be used in both training and sampling, what question does attributing the FID change to each separately answer? Are the mismatched configurations meaningful?

4- In Section 5, why does it matter that QQ and PP change during training while II stays roughly constant? Is this expected from theory or intuition, and what does it reveal about how structured diffusion affects FID?

5- Could the authors revise the abstract to be readable on its own, and state the takeaway of each table and figure explicitly, rather than only restating the numbers?

6- In Table 1, structured diffusion improves FID on three of four datasets, and the FFHQ result falls within error bars. How do the authors justify claiming that structured diffusion does not necessarily help? Could they add datasets, and check robustness across architectures, samplers, and metrics beyond FID?

2 comments
AuthorsOpenReview ↗

Response to Reviewer rMxz (R1–R6)

R1 — What the results establish. We cannot explain FFHQ degradation as a verified phenomenon: its matched Full−Reference effect is unresolved over training seeds (R6 below). The revised paper instead answers a narrower, testable question: which changes to a structured path affect measured FID at a given finite sampling budget? On CIFAR-100, common retiming has G−R=−4.025 [−6.343,−1.707] at NFE7, whereas centered redistribution has C−R=−0.709 [−1.231,−0.188] at NFE31 (paired 95% intervals, five seeds). These are separate scalar-reference contrasts, not proof that G and C swap direct superiority. They demonstrate budget-dependent measured responses, not a causal explanation of FFHQ's mean direction.

R2 — Intuition, frequency evidence, and use. Common retiming moves subspace log-noise schedules together; centered redistribution changes their relative schedules with zero rank-weighted mean log-noise shift. Zero trace does not preserve total noise power. To look beyond FID, we added a five-seed DCT diagnostic with 1,024 generated images per G/C–NFE condition. At NFE7, G's mean log-energy is closer to the real-image mean in all three bands for all five seeds, with spectral/FID direction agreement in four of five. At NFE31, high-band and FID directions agree in five of five seeds, but the paired mean high-band interval includes zero; low-band agreement is one of five. These are output correlates, not a demonstrated frequency-level cause of FID. The practical implication is to compare path coordinates at the intended NFE and inspect their output statistics.

R3 — Purpose of mismatched cross-evaluations. Matched model–sampler pairs remain the generation-quality comparisons. The off-diagonal cells ask a diagnostic question: does a factorial contrast among the same trained states depend on the common evaluator? It does: on AFHQv2 seed 3, QR=+1.979Q_R=+1.979 and QF=−1.582Q_F=-1.582. This response is not determined by the accounting identity. However, the symmetric T/S path-return term equals half the difference of two directional mismatch penalties; large opposition can reflect incompatibility. Cross-evaluations are diagnostic probes, not recommended deployment configurations or independent causal training/sampling effects.

R4 — Why training dynamics matter. The identity I=Q+PI=Q+P does not predict stable II with moving attribution. In seed 22, the sign of II is retrospectively certified from 70%, but the Q/PQ/P relation has no pre-final certificate; that absence does not establish a change. Seed 23 shows late sign reversals of both QQ and II. A separately frozen CIFAR-100 seed-24 test measures ΔQ=+1.9022\Delta Q=+1.9022 over 80–90% of its fixed 10-Mimg budget, exceeding the empirical 0.3629 generation-block variation radius; ΔI=+1.4417\Delta I=+1.4417 also changes. Thus final matched FID alone does not characterize checkpoint-wise conditional responses. We do not claim constant II magnitude or longer-budget convergence behavior.

R5 — Presentation and takeaways. We rewrote the abstract to state the question and empirical findings directly, tightened the Introduction and Sections 3–5, and adjusted Fig. 1 labels and the figure/table explanations. Table 1 now distinguishes descriptive dataset means from resolved effects; Tables 2–3 show which scalar-reference contrasts are supported at each NFE. Fig. 2's caption distinguishes conditional attribution from a constant-magnitude interpretation of II. These interpretations are also stated in the surrounding text.

R6 — Reliability and scope. Table 1's AFHQv2 and FFHQ mean Full−Reference differences are −0.235 [−0.637,+0.168] and +0.146 [−0.994,+1.285] (paired 95% intervals, three seeds each). Both include zero, so we no longer claim a verified FFHQ loss or a general failure of structured diffusion. The experiments cover 32×32/64×64 images; secondary metrics and a bounded Haar-projector check broaden diagnostics but do not establish robustness across larger datasets, architectures, or solver families.

I thank the authors for their rebuttal. However, most of my concerns remain unresolved. Mainly, concerns regarding the significance of the results (and them not matching the initial motivation that I found interesting), whether the analysis is actually insightful/useful, and the lacking presentation of the paper. I believe addressing all of these properly would require a significant amount of additional work and basically rewriting most of the paper. I am thus inclined to keep my score.

Reviewer_guaZOpenReview ↗
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Paper summary
  • This paper studies how assigning different noise schedules to different subspaces of a diffusion model’s representation affects generation quality, and whether the resulting change originates from training, sampling, or both.
    • Standard diffusion models share one scalar schedule across the representation;
    • OvaDiP generalizes this to an operator-valued path.
    • The paper makes three contributions.
      • (1) Structured path design: the path deformation is decomposed into a common retiming component and a centered structural redistribution component, which are studied through four factorial conditions (R, G, C, F).
      • (2) Training–sampling attribution: cross-evaluating trained models under different sampling paths is used to test whether small final FID differences conceal opposing contributions from training and sampling.
      • (3) Training dynamics: the attribution is tracked over training to examine whether it keeps evolving even when the final interaction appears stable.
Critical strengths
  • The design is interpretable. Decomposing the path deformation into common and centered components and evaluating them in a factorial R/G/C/F design cleanly separates the roles of the two components.
  • The paper points to a potentially important phenomenon: the trained-state and sampling-path terms can have large opposing contributions that leave only a small net FID difference. If robust, this suggests that a final generation metric alone may not reveal how a path modification works.
  • The authors are careful about the scope of their claims, and they provide code and closure checks that aid reproducibility.
Critical weaknesses
  • The central puzzle is neither statistically established nor resolved. I recognize that the paper positions itself as an analysis framework rather than a method, so I do not penalize the absence of uniform improvements. However, the analysis is motivated by the sign of the structured-path effect varying across datasets, and this premise is weakly supported.
  • The factorial interaction is the standard interaction contrast of a 2×22\times2 design, and the training–sampling decomposition is an algebraic identity that holds by construction. The path-return term involves evaluating trained models under non-matching sampling paths, so it may capture model–sampler incompatibility rather than a meaningful "sampling effect". Indeed, off-diagonal FIDs (roughly 20–36 in Tables 13–14) are far above diagonal ones (roughly 10-13), and the large opposing T/S terms may largely reflect this mismatch cost. The attribution also depends on the chosen sampler, which the paper itself acknowledges, so the conclusions are not intrinsic training or sampling effects.
Questions for authors
  • Can the authors show that the cross-dataset difference in Table 1 is real?
    • Can the attribution actually explain why FFHQ differs from the other datasets?
    • Experiments on larger-scale data (e.g., ImageNet-1k) would also help show that the findings extend beyond small benchmarks.
  • Please clarify the novelty relative to a standard 2×22\times2 factorial analysis and the telescoping identity.
    • That FID depends on both training and sampling is expected, so what new insight or actionable guidance does the framework provide?
  • How do you ensure the T and S terms are not dominated by train–sampler mismatch?
    • For instance, does the cancellation persist at smaller deformation amplitudes where mismatch is mild?
1 comment
AuthorsOpenReview ↗

Response to Reviewer guaZ (G1–G3)

G1 — Cross-dataset evidence and scale. The opposite AFHQv2 and FFHQ mean directions in Table 1 are not statistically established. At NFE63, paired Full−Reference FID is −0.235 [−0.637,+0.168] on AFHQv2 and +0.146 [−0.994,+1.285] on FFHQ (95% intervals, three independent training seeds each). Both intervals include zero, so we cannot claim a verified FFHQ degradation or explain a dataset-level difference that has not been resolved. CIFAR-100 at NFE31 gives −0.969 [−1.344,−0.594] across five training seeds. These results concern 32×32/64×64 images; ImageNet-1k, larger resolutions, and other architecture/solver families remain untested.

G2 — Novelty and actionable insight. We agree that the 2×2 interaction and the path-return identity are algebraic; neither is claimed as a new theorem. The contribution is the controlled measurement of responses those identities do not determine. Common retiming (G) and centered redistribution (C) can be varied separately. On CIFAR-100, G−R at NFE7 is −4.025 FID [−6.343,−1.707], whereas at NFE31 C−R is −0.709 [−1.231,−0.188] and G−R is −0.143 [−0.421,+0.135] (nominal paired 95% intervals, five seeds). These are Reference contrasts, not a confirmed direct G/C crossover: the NFE31 direct G−C interval includes zero, and the exact five-seed cross-budget sign-flip test gives p=0.125.

The complete 4×4 evaluations then reveal something matched FID and algebraic closure cannot show: among fixed trained states, the factorial contrast changes with the common sampler. On AFHQv2 seed 3, QR=+1.979Q_R=+1.979 but QF=−1.582Q_F=-1.582; the across-sampler within-seed range reaches 3.561 FID. Separately, a prospectively frozen CIFAR-100 seed-24 run measures a late ΔQ=+1.9022\Delta Q=+1.9022, exceeding its 0.3629 generation-block variation radius. The concrete guidance is diagnostic: compare G/C with Reference at the intended NFE, and check sampler sensitivity before interpreting QYQ_Y as a trained-state property. These observations are conditional, not causal stage identification or a universal path-design rule.

G3 — Mismatch and smaller amplitudes. The large opposing T/S terms cannot be interpreted independently of model–sampler mismatch. For the symmetric R/F comparison, define mR=JR∣F−JR∣Rm_R=J_{R\mid F}-J_{R\mid R} and mF=JF∣R−JF∣Fm_F=J_{F\mid R}-J_{F\mid F}. Then Ssym=(mR−mF)/2S_{\mathrm{sym}}=(m_R-m_F)/2, giving ∣Ssym∣≤(∣mR∣+∣mF∣)/2|S_{\mathrm{sym}}|\leq(|m_R|+|m_F|)/2. Thus large absolute path-return terms cannot persist if both directional mismatches are small. We have not retrained matched models at smaller deformation amplitudes; this bound does not show whether cancellation persists there. Section 4 now presents T/S as evaluator-conditioned accounting, not independent causal training/sampling contributions.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of Manuscript Revisions

We have revised the manuscript to clarify its main empirical findings and their scope. The title and abstract now reflect three connected analyses: controlled path interventions, sampler-dependent trained-state contrasts, and their evolution during training.

Path interventions (Sections 2–3). We added paired uncertainty estimates to distinguish observed FID differences from statistically supported effects. The opposite AFHQv2/FFHQ mean directions are not statistically resolved. A supplemental five-seed CIFAR-100 analysis also does not establish a direct G/C superiority crossover across sampling budgets.

Training–sampling attribution (Section 4). We completed the 4×4 model–sampler cross-evaluations and found that the factorial contrast among fixed trained states depends on the common evaluator. In AFHQv2 seed 3, it changes from QR=+1.979Q_R=+1.979 to QF=−1.582Q_F=-1.582. We also clarify the exact path-return identity and the role of model–sampler mismatch. These measurements do not independently identify causal training and sampling effects.

Attribution dynamics (Section 5). A separately frozen CIFAR-100 seed-24 experiment shows a change of +1.9022+1.9022 in the conditional trained-state contrast over 80–90% of the fixed training budget, exceeding the empirical generation-block variation radius of 0.36290.3629. The matched interaction also changes, so this is not evidence of a stable total concealing evolving attribution terms.

We additionally revised the Introduction, Conclusion, and Fig. 1 labels, and added supplemental frequency-domain diagnostics. Previously reported FID measurements remain unchanged. The results are limited to the evaluated finite systems.

For clarity, the original submission TL;DR remains visible, but its stronger suggestions of independent stage separation and a stabilized total interaction are superseded by the revised manuscript.

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