- Rating
- 2
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 1
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Paper summary
The paper introduces a fast multivariate time-series generator using a uniformly distributed spherical latent space with KoLeo regularization, enabling single-pass sampling without attention, adversarial training, or iterative methods.
Critical strengths
- Achieves competitive generation quality with a single forward pass, enabling 10–10,000× faster sampling.
- Uses a simple, reproducible architecture without attention, GANs, diffusion, or flow matching. 3, Introduces a uniformly distributed spherical latent space with KoLeo regularization instead of a Gaussian prior.
- Provides informative ablation studies identifying essential components and unnecessary complexities.
- Improves HAR classification accuracy from 0.841 to 0.906 when real training data is limited.
- Highlights limitations of standard evaluation protocols, particularly their inability to detect memorization.
Critical weaknesses
- The abstract should be revised to improve its clarity, conciseness, and overall readability, as the current version is somewhat confusing, unnecessary long sentences and lacks a clear presentation of the key points.
- The paper is not clearly written. There are several grammatical mistakes and sentence making issues. The description of the method should be improved.
- How do authors handle bad samples over the sphere? Nothing guarantees that D(M(Z_rand)) is distributed like the real data.
- The authors approved the evaluation scores generators against their own training data, so high fidelity could partly be memorization. Out-of-sample tests on Sines and MuJoCo help but don’t settle it.
- Competitiveness is measured against published numbers, and the authors note that their re-run baselines score worse. It makes the “state of the art” claim harder to verify. How can authors justify this?
- The use of MLP and LSTM backbones without explicit temporal structure in the latent space may limit the modeling of long-range dependencies and reduce generation quality for long sequences.
- Augmentation is evaluated only on HAR, using a small real dataset of 221 samples, and exhibits a performance gap of up to 3.2 percentage points compared with real data. The generalizability of these results to other tasks and domains remains unclear.
- The KoLeo regularizer pushes each point away from its nearest neighbour within a mini-batch. This is a local, batch-based criterion, so it does not guarantee uniform coverage of the sphere across the whole dataset, and its strength depends on the batch size and latent dimension. The loss weight may therefore need retuning when these change.
- Duplicate or near-duplicate points in a batch would make the logarithm term diverge, so numerical safeguards (e.g. a small epsilon) are needed.
- What is the motivation or reason for selecting these six datasets and using fixed training configurations (e.g., 2,000 epochs and a fixed batch size)? Are these choices justified by the characteristics of the datasets or supported by empirical evidence?
- The training cost and hyperparameter tuning effort are not sufficiently discussed or evaluated. How much training data the method needs?
- Ablation should be performed on more complex, high-dimensional or irregular real-world series.
- The evaluation would benefit from including recent baselines such as ImagenTime, COSCI-GAN, and TimeLDM, which have shown promising performance in time-series generation, particularly in latent-space modeling and inter-channel correlation preservation.
- Lack of novelty and limited technical contributions. The sphere latent, KoLeo regularizer and deterministic autoencoder with post-hoc sampling are all existing ideas. The contribution is mainly their combination.
- Code reproducibility is necessary to verify the results. I have some concerns regarding the outcomes. Authors must share the code or GitHub link (if any).
Questions for authors
Please see the section on weaknesses, e.g. W3, W5, W10, W11.
3 comments
Response to Reviewer ER47 (cont.)
W7: Augmentation on HAR only; small real set; gap to real data. For the scope of the HAR experiment, please see (D). The small real set is deliberate. We test whether our generator can supplement training when real data is extremely scarce, which is where augmentation matters most. Both the generator and the classifier use the same fixed 221-sample subset, so no further real data is used. Adding only half as many generated samples as there are real ones clearly raises test accuracy.
On the gap to real data: a gap is expected when a classifier never sees a real sample, and it is small in this setting. More importantly, synthetic samples can replace real ones almost without loss. When part of the train set is replaced by synthetic samples, accuracy stays close to that of the full real train set throughout. When the same samples are instead removed, accuracy falls sharply once very little real data remains, and reaches chance level without real data (Fig. 4, left).
W8: KoLeo is local and batch-based; sensitivity to batch size and latent dimension. Locality is deliberate (A). KoLeo targets the same uniform distribution as a global criterion such as the MMD, but pushes hardest where latents crowd, and fills gaps between neighbors directly. Coverage over the whole dataset is not guaranteed by a batch-based loss, so we measure it. The new holes ratio is computed on the full training set, against prior draws of the same size. For our model, it shows that the latents cover the sphere more evenly than a random sample would, on four of the six datasets with latent noise and on all six without. On sensitivity: we keep the batch size fixed, while the latent dimension varies by two orders of magnitude across datasets. The ablation sweeps the KoLeo weight on all six datasets, and the best weight lies within a factor of 10 of our shared 1e-2 on every one.
W9: Numerical safeguards. We agree, and our implementation already includes them. It follows the KoLeo implementation of DINOv2: epsilon = 1e-8 is added to the nearest-neighbor distance before the logarithm, and is also used when normalizing and computing distances. Each term is therefore bounded by -log(epsilon) ≈ 18.4, even for exact duplicates. Each batch is also drawn without replacement. All of our runs, including the 1,040 models of the new ablation, trained without numerical problems. We omitted epsilon from Eq. 5 for readability; the code includes it (W15).
W10: Choice of datasets and fixed training configurations. For the datasets, please see (C). The fixed configuration is deliberate, and Section 4.2 now motivates it. The standard suite has no held-out validation split, so any hyperparameter tuned per dataset is tuned on the evaluation criterion itself. To keep this to a minimum, we tuned the full setup once, on Sines, and transferred it, sweeping only the latent size per dataset. Two further choices were introduced only where training otherwise failed: a cosine learning-rate schedule (MuJoCo) and LSTM backbones (Energy). A setup that transfers with this little tuning is also the stronger result. The new ablation supports the transfer: on every dataset, the best KoLeo weight lies within a factor of 10 of the shared weight (Appendix E.2). Out-of-sample scores on Sines and MuJoCo show that this tuning did not substantially affect generalization (Appendix E.1).
W11: Training cost, tuning effort and data requirements. We agree that these are important questions. To our knowledge, they are rarely studied in the time series generation literature, and characterizing how much data our approach requires is part of our future work. Within this paper, we address them where we can. Section 4.2 describes our deliberately minimal tuning protocol (see W10). On data requirements, the low-data HAR experiment trains both the generator and the classifier on only 221 real samples, and the generated samples still clearly raise accuracy.
W12: Ablation on more complex data. The new ablation now covers all six datasets, including the high-dimensional Energy (28 channels) and fMRI (50 channels) (A). Irregularly sampled series are outside the scope of our method and benchmark (see Uav3, W5).
Response to Reviewer ER47 (cont. b)
W13: Missing baselines (ImagenTime, COSCI-GAN, TimeLDM). These methods are relevant, but we cannot compare against every generator, so we selected baselines by explicit criteria (Appendix D.3). We aimed to cover each family with one well-established and one recent method: GANs (TimeGAN, GT-GAN), VAEs (KoVAE), diffusion (Diffusion-TS, PaD-TS), flow matching (SMF, PrismFlow) and discrete-token transformers (SDformer). The suggested methods belong to families that are already represented: COSCI-GAN is a GAN, and ImagenTime and TimeLDM are diffusion models. We did consider ImagenTime. We chose Diffusion-TS as the established diffusion baseline because it reports results on all six datasets and is the diffusion baseline used by the most recent method in our comparison, PrismFlow.
W14: Novelty. Please see (B).
W15: Code. We agree that code is necessary to verify the results. We have added an anonymized codebase as supplementary material. It contains the code to train every model in the paper and compute its reported scores, with one command per result, including all 1,040 models of the new ablation. We would be glad to address the reviewer's specific concerns about the outcomes if the reviewer could point us to them.
Response to Reviewer ER47
We thank the reviewer for the detailed review.
W1, W2: Abstract, writing and method description. We have revised the abstract. It now opens with the problem and motivation, uses shorter sentences, and states the key findings more directly. We found that our citation commands rendered parenthetical citations as in-text ones throughout, which made many sentences read as broken. This is fixed. We have also proofread the full paper. The Method section (Section 3) now opens with a notation paragraph and states the shape of every quantity. It removes overloaded symbols, and writes the projection, the generator, both loss terms and the latent noise as explicit equations.
W3: Bad samples; no guarantee that generated samples are distributed like the data. We do not filter or reject samples: every reported score is computed on all generated samples, as many as there are training samples. Instead, the model is designed so that bad samples are rare. The new Section 6.1 explains why we expect decoded draws from the prior to be distributed like the data (A). Bad samples arise as blur, where latents overlap, or from holes, where the prior has no training latents. The deterministic encoder is not penalized for keeping inputs apart. The projection places every latent on the support of the prior. KoLeo spreads the latents uniformly, which is equivalent to minimizing their divergence from the uniform prior. No generator offers a formal guarantee here, but the new ablation confirms this empirically. On every dataset, our model leaves fewer holes than the MMD-based variants. On most datasets, its prior draws lie closer to a training latent than the training latents lie to each other, at a low reconstruction error.
W4: Memorization. We agree, and highlighting this is part of our contribution. The standard suite scores generators against their own training data, and we show that it is largely blind to memorization (Appendix E.1). This applies to every method in the comparison, including ours. Sines and MuJoCo are the only benchmark datasets with a known generating process, so they are the only ones on which we can evaluate on fresh data at all. There, our scores barely change out of sample, which shows that tuning on the training set did not compromise generalization. As the reviewer notes, and as we state in the paper, this does not settle memorization. We name this as a limitation in the Conclusion.
W5: Comparison with published numbers; re-run baselines score worse. We apologize for the confusion. "Self-reported" means the scores that each method's authors published for their own method. We did not re-run any baseline. The re-run scores we mention come from other papers: PaD-TS and SMF re-ran Diffusion-TS and report worse scores than Diffusion-TS reports for itself, in most overlapping cells. This observation motivates our choice. Comparing against self-reported scores is the conservative option, because it compares our results with each baseline at its best. Re-running the baselines ourselves would likely make them look worse, so it would make our claim easier to support, not harder. We checked the public code of every baseline except PrismFlow, which has none, and confirmed that its self-reported scores were produced on the same datasets with a compatible evaluation protocol (Appendix D.3). A footnote in the Introduction now defines self-reported scores, and Section 4.3 states that we do not re-run baselines and why.
W6: MLP and LSTM backbones and long-range dependencies. We agree for the MLP backbones. Their latent has no explicit time axis, so temporal structure is encoded only implicitly. The LSTM backbones are different. Their latent keeps a compressed time axis, and the projection only rescales it. We use them for the 128-step HAR experiments, where a classifier trained only on our synthetic samples comes close to one trained on real data. That said, we see the competitiveness of the MLP models as a finding in itself. On four of the six benchmarks, a latent without any time axis is enough to be competitive. This suggests that these benchmarks do not require a latent that explicitly models temporal dynamics, and that more temporally demanding benchmarks are needed. Enforcing temporal structure in the latent more directly is part of the future work we name in the Conclusion.