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Under review as a conference paper at ICLR 2027

Understanding Prediction Target, Time Sampling, and Model Capacity in Diffusion Models

Abstract

Denoising diffusion models require several coupled design choices: what the network predicts, how timesteps are sampled, and how much capacity the architecture provides. Three recent empirical findings shed light on how to make these choices: (i) clean data prediction can have higher generation quality than noise or velocity prediction; (ii) sampling timesteps from a logit-normal distribution can outperform uniform sampling; and (iii) generation quality can peak at an intermediate model capacity. However, a theoretical understanding of these observations, and particularly of how the three choices interact, remains limited. In this paper, we show that theoretical counterparts of all three observations arise in a tractable linear model with Gaussian data and a time-gated predictor. Specifically, our spectral analysis reveals how prediction targets, timestep sampling, and model capacity jointly determine which spectral components of the data are represented by the model and, in turn, shape the generated distribution, a principle we refer to as spectral selection. This analysis further shows that the optimal design choices depend on the spectral structure of the data. We provide empirical support for our theoretical findings on synthetic and real data.

Primary area:
generative models
Keywords:
Denoising Diffusion Model, Prediction Target, Timestep Sampling, Model Capacity, Generalization, Linear Model, Spectral Analysis

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_GpLmOpenReview ↗
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2
Confidence
3
Informativeness
1
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2
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Paper summary

This paper investigates how prediction targets, timestep sampling, and model capacity affect diffusion generation. It studies a simplified Gaussian setting with a linear model that shares a bottleneck across time. The main idea is that limited capacity forces the model to select certain covariance directions; prediction targets and timestep weights influence this selection and the behavior of omitted directions. It derives optimal targets, bottleneck sizes, and sampling distributions under specific assumptions, plus a worst-case error result near x-prediction. Synthetic experiments and CelebA-HQ experiments with JiT reproduce familiar trends: x-prediction, nonuniform sampling, and intermediate bottlenecks are helpful.

Critical strengths

The strength is how it connects what the model learns to what it actually generates. The spectral analysis makes clear why a lower training loss doesn’t necessarily mean better generation, and shows how prediction targets, timestep sampling, and limited capacity interact within one tractable framework.

Critical weaknesses
  1. Some findings have been studied in prior work. [1] already derive dimension-dependent optimal prediction targets. [2] provide Gaussian velocity and covariance formulas matching key parts of this analysis. [3] connect covariance spectra to endpoint error and inference schedule optimization. The paper needs to explain what additional theoretical insight its shared-bottleneck constraint provides.

  2. Weak evaluation. the experiments mostly reproduce familiar trends without directly testing the new mechanism. The datasets benchmarked on are overall simple. There is no clear measurement of learned-subspace alignment or direct test of the proposed optimal sampling results, leaving the main theoretical contributions weakly validated.

  3. Restrictive assumptions. Gaussian data and a linear predictor make covariance structure sufficient to describe the entire problem. Real diffusion models learn nonlinear, multimodal distributions. The paper offers little evidence that its conclusions survive beyond this simplified setting, making it unclear whether the proposed mechanism explains the real-data results.

[1] Revisiting Diffusion Model Predictions Through Dimensionality [2] An Analytical Theory of Spectral Bias in the Learning Dynamics of Diffusion Models [3] Spectral Analysis of Diffusion Models with Application to Schedule Design

Questions for authors

none

1 comment

We sincerely thank the reviewer for the careful reading and constructive feedback. Below, we address each point.

W1. Additional theoretical insight compared to cited works

We thank the reviewer for pointing out these connections. We agree that the cited works [1, 2, 3] also study Gaussian data and linear settings theoretically, and thus share some aspects of the results. However, we would like to emphasize that our distinct theoretical insights lie not in deriving these baseline properties, but in characterizing how prediction target, timestep sampling and model capacity jointly shape generation quality.

In particular, as we discussed in lines 111-118, [1] compares prediction targets using training loss, whereas we compare them by characterizing the Wasserstein distance of the generated distributions. This seemingly subtle difference yields fundamentally distinct insights: in a time-independent linear setting as in [1], a lower training loss can correspond to a larger endpoint Wasserstein error, and this error can even diverge (see Appendix A). Thus, comparing training losses alone across different targets does not reliably indicate which prediction target is superior.

In addition, while [2] focuses on how the eigenvalues govern the training speed along each direction during optimization, ours characterizes which directions are selected at the training loss minimizer. Furthermore, [3] provides theoretical insights into inference-time noise schedule design that complement our analysis of timestep sampling during training. We have cited these works and added the analysis regarding [1] to Appendix A of the revised manuscript.

W2. Weak empirical evaluation of the new theoretical mechanism

We agree with the reviewer that our experiments do not sufficiently validate the theoretical findings. To explore whether our findings also arise beyond theoretical settings, we trained nonlinear models on Fourier data while jointly varying the three design choices rather than conducting separate sweeps. Following Gagneux et al. (2026), we constructed each data sample from a weighted sum of 16 Fourier modes. This setting provides a controlled spectral structure in which individual Fourier modes can be assigned different coefficient variances, allowing us to directly examine which spectral components are prioritized by the trained model. We compared relative reductions in prediction loss across modes with different coefficient variances and reported the results in Figure 3.

For xx-prediction (α=1\alpha = 1) with a bottleneck width of 4, the model substantially reduced prediction loss in the higher-variance components, with little reduction in the lower-variance components. Which components the trained model prioritized was jointly affected by the three design choices. We have added these results and training details to Appendix F.2 of the revised manuscript.

Furthermore, we conducted experiments to test the optimal density proposed in Eq. (21). We trained the model on the synthetic setting of Appendix F.1 under four different timestep distributions, including the distribution in Eq. (21). We used α=0.99\alpha = 0.99, spectrum λi=i−1\lambda_i = i^{-1}, dimension D=d=10D = d = 10, and width m=5m = 5, and evaluated the generated distributions at the same excess loss of η=10−3\eta = 10^{-3}.

Timestep distributionW22\mathcal{W}_2^2
Eq. (21)0.6105
Uniform0.6104
Logit-normal ((μ,σ)=(0,1)(\mu, \sigma) = (0, 1))0.6172
Logit-normal ((μ,σ)=(0.8,1)(\mu, \sigma) = (0.8, 1))0.6101

Although the sampling distribution in Eq. (21) exhibits generation error comparable to the other choices rather than showing a clear empirical advantage, this result is not inconsistent with Theorem 6, since the theorem states that this density minimizes the worst-case generation error over all predictors with excess loss at most η\eta, whereas practically trained predictors may not correspond to the worst case.

W3. Gaussian data and linear network are restrictive assumptions

We agree that assumptions do not capture all aspects of realistic settings. However, by providing tractable analysis and isolating specific mechanisms in diffusion models, Gaussian data and linear settings serve as standard theoretical testbeds [1, 2, 3, GMM+26]. Such theoretical analyses can offer insight into the behavior of more complex nonlinear models. In this regard, we conducted additional experiments showing that several qualitative trends predicted by our theory appear to transfer to nonlinear settings, as detailed in our response to [W2].

Still, extending our theoretical analysis to nonlinear predictors, for example through random feature models, remains an exciting direction for future work.

[GMM+26] Gagneux, Martin, Gribonval, & Massias. Training Flow Matching: The Role of Weighting and Parameterization. ICLR Workshop on DGM, 2026.

Reviewer_2c2iOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
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Paper summary

The submission studies the interaction among prediction target, timestep sampling, and model capacity in diffusion/flow-matching models. In a tractable setting with Gaussian data and a time-gated, rank-constrained linear predictor, the authors introduce a spectral score that quantifies the training-loss reduction associated with representing a covariance eigendirection. They show that a population-loss minimizer selects the directions with the largest scores and characterize how the resulting generated covariance depends on the selected directions and prediction parameterization. Further theoretical results examine timestep weighting, target preferences, and capacity-dependent generation error. Synthetic experiments and experiments on CelebA-HQ provide empirical support.

Critical strengths

--The paper addresses an important practical question: why prediction targets, timestep distributions, and capacity interact in generative training.

--The Gaussian, low-rank model offers an interpretable mathematical setting in which training objectives and generated distributions can be analyzed explicitly.

--Theorems 2--5 move beyond subspace selection to characterize generated variances, endpoint-optimal timestep sampling, and the dependence of favorable prediction targets and bottleneck widths on data structure. These generation-level consequences are the most distinctive aspect of the theoretical contribution.

--The paper includes both controlled synthetic tests and real-image experiments.

Critical weaknesses

Insufficient positioning relative to classical spectral methods. The principal characterization uses the eigendecomposition of the data covariance and a rank-constrained linear predictor. For xx-prediction, the selected subspace consists of leading covariance eigendirections, closely resembling PCA and classical low-rank approximation. The related-work discussion does not sufficiently distinguish this spectral-selection mechanism from established PCA and reduced-rank regression arguments. This does not make the paper merely a restatement of PCA: the target- and sampling-dependent scores and, especially, the generation-level consequences in Theorems 2--5 are more distinctive. The authors should more precisely separate the classical rank-constrained selection principle from the new diffusion-specific implications.

Incomplete discussion of spectral diffusion precedents. The paper would benefit from engagement with covariance- and spectrum-aware generative modeling, including \emph{Spectral Diffusion Processes} (Phillips et al., 2022; \url{https://arxiv.org/abs/2209.14125}) and \emph{Structured Drift Design for Denoising Diffusion Models} (Taheri et al., 2026; \url{https://arxiv.org/abs/2606.03360}). These papers have different objectives and should not be treated as proving the submission's theorems. Nevertheless, they illustrate relevant prior uses of spectral structure in diffusion modeling. A careful comparison of assumptions, objectives, and conclusions would improve the novelty argument without implying that these works already establish the submission's results.

Restricted modeling assumptions. The analysis assumes centered Gaussian data and a linear time-gated predictor with an explicit bottleneck rank. These assumptions are reasonable for an exact analysis, and I do not view a full extension to Gaussian mixtures or nonlinear models as necessary for acceptance. However, the authors should distinguish conclusions that rely on simultaneous diagonalization and population-optimal training from mechanisms they expect to remain relevant in practical nonlinear models.

Mechanistic interpretation of empirical results. The image experiments demonstrate trends in generation quality, but those trends alone do not establish that neural models are selecting covariance directions according to the proposed scores. Where feasible, more direct measurements of representation alignment or spectral changes as the target and timestep distribution vary would help distinguish the proposed mechanism from alternative explanations based on optimization or architecture.

Interpretation and practical relevance of Theorem 3. The endpoint-optimal timestep-sampling theorem is a valuable bridge between training loss and generation error, but it establishes the existence of a suitable concentrated logit-normal density and of a favorable population-loss minimizer. It does not establish that commonly used sampling distributions are near-optimal or that finite-sample gradient-based training reaches the desired selection. A clearer discussion of how this existence result informs practical sampling choices would strengthen the contribution.

Questions for authors

How does Theorem 1 relate formally to weighted or time-integrated reduced-rank regression, and which aspects of Theorems 2--5 are not captured by that classical viewpoint?

--For α=1\alpha=1, the score ordering agrees with covariance-eigenvalue ordering. How do the authors distinguish this observation from PCA/Karhunen--Lo`eve truncation, and what is the closest prior result for α≠1\alpha\neq 1?

--How does the analysis relate to prior spectral diffusion constructions, particularly Phillips et al. (2022), and to covariance-aware drift design such as Taheri et al. (2026)?

--Can the authors provide more direct evidence, even in a controlled neural setting, that changing the target or timestep distribution alters learned representations in the direction predicted by the spectral scores?

--For Theorem 3, how should one interpret the sufficiently concentrated logit-normal construction in relation to practical sampling distributions and optimization? Can the authors give an illustrative parameter choice or sensitivity analysis?

4 comments

We sincerely thank the reviewer for the careful reading and constructive feedback. Below, we address each point.

Q1, Q2, W1. Insufficient positioning relative to classical spectral methods

We thank the reviewer for highlighting this connection. As the reviewer correctly noted, at each fixed tt, the training problem reduces to classical reduced-rank regression. Specifically, for xx-prediction (α=1\alpha = 1), the optimal rank-mm subspace coincides with the leading PCA/Karhunen–Loève subspace of the data at every tt. For other targets (0<α<10 < \alpha < 1), the target yαy^\alpha combines data and noise, and therefore the optimal rank-mm subspace can differ from the data Karhunen–Loève subspace; rather, predicting yαy^\alpha from ztz_t for each tt is an instance of the generalized Karhunen–Loève transform [HL98]. Nevertheless, the optimal subspace can vary with tt in such a setting, whereas our bottleneck predictor enforces a single shared subspace across all tt.

Furthermore, we agree that Theorem 1 and Theorems 2–5 should be clearly separated: while the former shares key principles with classical reduced-rank regression, the latter characterize the diffusion-specific generation dynamics. In the revision, we have cited the related literature in Sections 3 and 4.2 and made this separation explicit in Section 4.3.

[HL98] Hua & Liu. Generalized Karhunen–Loeve Transform. IEEE Signal Processing Letters, 1998.

Q3, W2 Missing citation and positioning relative to spectral diffusion precedents

We thank the reviewer for bringing these works to our attention. We agree that these works are related to our work. Our main distinction is that we do not explicitly prescribe spectral directions through either basis truncation or modification of the forward process. Instead, under the standard forward process, we show how the prediction target, timestep sampling, and model capacity jointly induce an implicit selection of eigendirections at a training-loss minimizer, depending on the covariance spectrum.

More specifically, Phillips et al. (2022) select directions by truncating a kernel basis, whereas our rank-constrained predictor implicitly learns the subspace during training. Consequently, their generation along truncated directions has zero variance, while ours retains an endpoint variance of ((1−α)/α)2((1-\alpha)/\alpha)^2 for 0<α<10 < \alpha < 1. Taheri (2026), on the other hand, modifies the forward process using the data covariance to explicitly design direction-dependent contraction rates, whereas we retain the standard forward process and obtain direction-dependent selection through the training problem itself. In the revision, we have discussed and clarified these distinctions in Appendix C.3.

Q4, W4. Spectral selection in neural models

To test whether the theoretical findings in tractable settings persist in a controlled nonlinear setting, we trained bottleneck MLPs on the Fourier images adapted from Gagneux et al. (2026). This setting provides a controlled spectral structure in which individual modes can be assigned different coefficient variances, allowing us to directly examine which spectral components are prioritized by the trained model. The results are qualitatively consistent with our theory. In particular, as shown in Figure 3, nonlinear models trained with larger α\alpha tended to prioritize higher-variance components, while models with wider bottlenecks also learned lower-variance components; this prioritization further depends on the timestep sampling. We revised the manuscript and added details of the experiments in Appendix F.2.

Q5, W5. Interpretation and practical relevance of Theorem 3

We thank the reviewer for raising this point. In practice, a widely used timestep sampling distribution is the logit-normal density, and Theorem 3 establishes the existence of the logit-normal density for which a loss minimizer attains the optimal endpoint error. Since sweeping the mean and variance of logit-normal densities is already standard in practice, a further practical implication is that changing the prediction target or model capacity can warrant retuning the timestep distribution, even when the data distribution is fixed.

We believe that Theorem 6 has more practical relevance, although it relies on certain conditions. In practice, training typically leaves a nonzero excess loss, and Theorem 6 shows that the optimal sampling under vv-loss in those cases is unimodal; indeed, the logit-normal density is unimodal and often yields superior generation quality. Reproducing this loss weighting through timestep sampling under xx- or ϵ\epsilon-loss would require non-normalizable densities, which is practically infeasible. Therefore, we believe that these findings may help inform practical sampling choices.

W3. Relation to nonlinear models

We thank the reviewer for highlighting the need to carefully distinguish our theory from expectations for nonlinear models. While our additional experiments in controlled nonlinear settings detailed in [Q4, W4] provide empirical evidence that several qualitative trends carry over to nonlinear models, we agree that claims implying a direct transfer should be toned down. Accordingly, we have revised the manuscript in lines 530–532, as well as in Section 7.

Thank you for the responses. I appreciate the clarifications on the connection to reduced-rank regression / Karhunen–Loève and the distinctions from Phillips et al. (2022) and Taheri et al. (2026), as well as the additional nonlinear experiments. These points have partially addressed my novelty concern.

I would consider increasing my score to 3, yet I encourage the authors to consider that their revised manuscript includes a more comprehensive literature review and a systematic comparison with classical spectral methods and related covariance-aware generative work. In particular, this comparison should clearly establish which spectral-selection results reduce to existing analyses and which constitute genuinely new diffusion-specific contributions.

We thank the reviewer for the follow-up and agree that these distinctions should be explicitly presented in the manuscript, rather than only explained in our response. We have now incorporated the relevant comparisons and citations directly into Sections 2 and 4 of the revised manuscript, with all changes highlighted in cyan.

In Section 4, we now explain that the training problem we consider at each fixed timestep reduces to classical reduced-rank regression [I75] and takes the form of the generalized Karhunen–Loève transform studied in [HL98], whereas our predictor class shares its bottleneck subspaces across timesteps. We also clarify that, for xx-prediction, the subspace selected by the training-loss minimizer coincides with the leading PCA subspace [H33]. In addition, we clarify the diffusion-specific generation dynamics in Section 4.3. We convert the prediction from the learned predictor into a velocity field and solve the ODE to characterize the generated distribution along both represented and omitted directions.

Furthermore, we revised the related work in Section 2 to discuss how the covariance structure of the data can be used and studied in diffusion models: Phillips et al. (2022) explicitly truncate the generation subspace based on a chosen kernel, which corresponds to selecting a data covariance subspace when the data covariance kernel is used, whereas we characterize how the subspace is implicitly selected depending on the three design choices. Moreover, Taheri (2026) explicitly uses the covariance to design the direction-wise speed of the forward diffusion process. In addition, [WP25] analyze the connection from training dynamics to generation with Gaussian data and a linear predictor by showing that, under gradient-flow training, the generated variances converge faster to those of the data along leading covariance eigendirections.

[H33] Hotelling. Analysis of a Complex of Statistical Variables into Principal Components. Journal of Educational Psychology, 1933.

[I75] Izenman. Reduced-Rank Regression for the Multivariate Linear Model. Journal of Multivariate Analysis, 1975.

[WP25] Wang and Pehlevan. An Analytical Theory of Spectral Bias in the Learning Dynamics of Diffusion Models. Advances in Neural Information Processing Systems, 2025.

Reviewer_kwzZOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

This paper studies how prediction targets, timestep sampling, and model capacity jointly affect generation in diffusion models. In a tractable setting with Gaussian data and a linear time-gated predictor, the authors derive spectral scores that determine which covariance eigendirections a training-loss minimizer represents under a bottleneck constraint. They then characterize the generated covariance, showing that represented directions recover their data variances while omitted directions have a prediction-target-dependent default variance. This analysis yields results on preferred prediction targets, timestep sampling, and model capacity. The paper further studies how residual training errors propagate to generation error. Synthetic experiments support the theoretical predictions, while CelebA-HQ experiments reproduce related qualitative trends.

Critical strengths

Unified Analysis of Training and Generation: The paper provides a coherent framework connecting prediction targets, timestep sampling, and bottleneck capacity through spectral selection. The analysis goes beyond comparing regression losses by explicitly characterizing the generated endpoint distribution. The analysis shows that selected directions recover their data variances. Omitted directions instead have variances determined by the prediction target. This helps explain how prediction parameterizations affect generation under limited capacity.

Analysis Beyond Exact Loss Minimization: Section 6 addresses an important limitation of the exact-minimizer analysis: under x-prediction, spectral selection is independent of timestep sampling. By analyzing how residual prediction errors affect generation, the paper identifies an additional mechanism through which timestep sampling matters. The appendix also explicitly discusses the restrictions of this result, including its exclusion of exact x-prediction and the fact that logit-normal densities do not satisfy its reciprocal-integrability condition.

Critical weaknesses

Limited Validation of the Proposed Mechanism Beyond the Tractable Setting: The intermediate-capacity optimum derived for x-prediction relies on evaluating against a clean distribution that excludes nuisance directions present in training. When the evaluation distribution equals the training distribution, full width recovers the training covariance exactly and is therefore optimal within the theoretical model (Appendix C.2, "The boundary target and full width"). The CelebA-HQ experiments reproduce a qualitative capacity optimum but do not establish an analogous signal/nuisance decomposition or directly measure spectral selection. Moreover, these experiments vary the three design choices separately rather than testing their predicted interactions. Although the paper acknowledges the limitations of its tractable setting, the experiments leave open whether the proposed mechanism explains the observed behavior of nonlinear image models.

Insufficient Specification of Endpoint Stabilization and Experimental Details: Appendix E.2 states that all parameterizations use a common stabilized velocity-space training objective but does not provide its formula or stabilization parameters. This matters because, depending on the timestep density, the population velocity loss can diverge under exact x-prediction when positive-variance directions are omitted, as discussed in Appendix D. Any timestep truncation, denominator clipping, or additional loss weighting could therefore affect the comparison between prediction targets and its connection to the theory. Appendix E.1 also omits details such as the time-feature construction, time-embedding dimension, optimizer, and numerical integration settings. These omissions limit reproducibility.

Questions for authors

Endpoint Stabilization: What is the exact stabilized velocity-space objective used in the experiments? Please specify any timestep truncation, denominator clipping, or additional loss weighting and its parameters. How sensitive are the prediction-target comparisons to these choices?

Connection to Real-Data Behavior: What evidence connects the intermediate-capacity optimum on CelebA-HQ to the signal/nuisance mechanism in the theory? Could the authors test a predicted interaction between prediction target, timestep sampling, and capacity, rather than only their separate qualitative trends?

Evaluation of the Derived Sampling Density: How does the sampling density in Eq. (21) perform relative to uniform and logit-normal sampling in the synthetic regime covered by Theorem 6? This comparison would help distinguish empirical validation of the derived density from qualitative agreement about emphasizing intermediate timesteps.

Reproducibility and Variability: Please provide the missing synthetic training and time-embedding settings, as well as the real-data optimization details. Are results from independent training seeds available for the capacity comparison between ranks 48 and 192? If not, please clarify how this uncertainty limits the conclusion about an intermediate-capacity optimum.

2 comments

We are grateful for the reviewer’s insightful feedback and positive assessment, which helped us present our contribution more clearly. Below, we address each point.

Q1, W2. Endpoint stabilization and experimental details

We thank the reviewer for pointing out this omission. For xx-prediction, i.e., α=1\alpha = 1, in the CelebA-HQ experiments, following the formulation in JiT (Li and He, 2026), we use the training objective with a denominator floor,

E[∥f(zt,t)−x∥22max⁡1−t,0.052].\mathbb{E}\left[\frac{\lVert f(z_t,t)-x\rVert_2^2}{\max\\{1-t,0.05\\}^2}\right].

We also apply the same denominator floor during generation to avoid division by near-zero values. This stabilization is not necessary for 0<α<10 < \alpha < 1, since the velocity-conversion denominator dα(t)=α(1−t)+(1−α)td_\alpha(t) = \alpha(1-t) + (1-\alpha)t in Eq. (5) is lower bounded away from zero for every t∈(0,1)t \in (0,1), unlike in the case α=1\alpha = 1.

In the synthetic experiments, we use 256 sinusoidal time features constructed from 128 frequencies logarithmically spaced from 10−110^{-1} to 10210^2. We train for 80,000 optimization steps using Adam with an initial learning rate of 3×10−33 \times 10^{-3}, cosine learning-rate decay. We have added these details to Appendix F of the revised manuscript.

Q2, W1. Limited validation of the proposed mechanism

We agree that the CelebA-HQ experiments do not sufficiently validate the theoretical findings. To explore whether our findings arise in nonlinear settings, we trained nonlinear models on synthetic Fourier images while jointly varying the prediction target, timestep distribution, and bottleneck width. Following Gagneux et al. (2026), we constructed each image from a weighted sum of 16 Fourier modes. This setting provides a controlled spectral structure in which individual modes can be assigned different coefficient variances, allowing us to directly examine which spectral components are prioritized by the trained model. We compared relative reductions in prediction loss across modes with different coefficient variances and reported the results in Figure 3.

For xx-prediction (α=1\alpha = 1), the trained model with a bottleneck width of 4 achieved a larger loss reduction in the higher-variance group than in the lower-variance groups. Which groups the trained model prioritizes varied with the prediction target, timestep distribution, and bottleneck width. We have added these results to Section 7 and training details to Appendix F.2 of the revised manuscript.

Q3. Comparison of the timestep density in Eq. (21)

We thank the reviewer for this suggestion. We trained the model on the synthetic setting of Appendix F.1, under four different timestep distributions, including the distribution in Eq.(21). We used α=0.99\alpha = 0.99, spectrum λi=i−1\lambda_i = i^{-1}, dimension D=d=10D = d = 10, and width m=5m = 5, and evaluated the generated distributions at a same excess loss of η=10−3\eta = 10^{-3}.

Timestep distributionW22\mathcal{W}_2^2
Eq. (21)0.6105
Uniform0.6104
Logit-normal ((μ,σ)=(0,1)(\mu, \sigma) = (0, 1))0.6172
Logit-normal ((μ,σ)=(0.8,1)(\mu, \sigma) = (0.8, 1))0.6101

Although the sampling distribution in Eq. (21) exhibits generation error comparable to the other choices rather than showing a clear empirical advantage, this result is not inconsistent with Theorem 6. The theorem states that this density minimizes the worst-case generation error over all predictors with excess loss at most η\eta, whereas practically trained predictors may not correspond to the worst case.

Q4. Training details and variation across seeds

We thank the reviewer for raising this point. These details were specified in the code included in the supplementary material but were omitted from the manuscript. To quantify variability across runs, we repeated the CelebA-HQ experiments with five seeds, which reproduces the reported trend with rank 48 yielding a lower FID than rank 192 (11.78±0.3611.78 \pm 0.36 vs. 12.66±0.5712.66 \pm 0.57). We have added these results and the optimization details to Appendix F.3 of the revised manuscript.

Thank you for the clarifications and additional experiments. The explicit stabilization objective, controlled nonlinear Fourier experiments, and five-seed capacity comparison address most of my concerns. I also agree that the results for Eq. (21) do not contradict its worst-case guarantee.

The sensitivity to the stabilization threshold and the connection to the CelebA-HQ capacity optimum remain limitations, but they do not change my overall assessment. I maintain my original recommendation of Weak acceptance.

Comments on the paper

1 comment

Dear reviewers,

This is a friendly reminder to read the authors’ rebuttals and post your responses by Nov 18. Please briefly indicate which concerns have been addressed and which remain unresolved. Even if your overall assessment remains unchanged, please provide a brief response to the authors. Please also update your reviews and scores as appropriate. Thank you for your time and effort!

AC.

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