- Rating
- 3
- Confidence
- 4(+1)
- Informativeness
- 3
- Presentation
- 2
- Soundness
- 3
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Paper summary
The paper proposes Cross-View Time-Frequency Diffusion (CrossTF) for extreme-aware time-series generation. The paper reports average improvements of 26.1% in extreme fidelity and 7.4% in aggregate overall performance over the strongest baselines. The paper is well written, and its experimental evaluation is extensive.
Critical strengths
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Exploiting discrepancies between time- and frequency-view denoisers provides a compelling direction for refining extreme behavior. The asymmetry analysis, window analysis, and same-view ensemble comparison provide useful empirical motivation for this design.
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The experiments cover diverse domains, generic and extreme-aware generators, and single-view ablations. These findings support a substantive benefit for reproducing extreme severity.
Critical weaknesses
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Appendix D.3 states that baselines train on each dataset's full array; the released code likewise trains the CrossTF branches, optimizes fusion, and evaluates fidelity against the same complete real dataset. Consequently, the real data used for the predictive evaluation have already been available to the generator, and the current protocol does not establish utility on unseen real sequences. The authors should provide a clear train/validation/test protocol.
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The same 18-step schedule and final-six-step window are used on all seven datasets. However, they do not show whether the chosen window is similarly suitable for each dataset, or whether its benefits persist when the window boundary, sampling schedule, or number of steps changes.
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Sections 2.3 described the EDM implementation, but the paper does not explain why its preconditioning and sampler are particularly suitable for combining the two views or test whether the cross-view benefit persists with another diffusion backbone.
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Table 2 reports a single Extreme Fidelity and Overall Performance score per dataset without stating the aggregation formula or explicitly listing the metrics entering each score. This omission makes the headline 26.1% and 7.4% improvements harder to interpret and verify.
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In Table 3, FIDE and HeavyDiff perform worse on most extreme-fidelity metrics than a general-purpose baseline such as ImagenTime. Appendix D.3 describes substantial intervention in these comparisons: FIDE's implementation was repaired, HeavyDiff was reimplemented, and E4GEN's event threshold was changed. It is difficult to determine whether their weak results reflect the methods, the adaptations, or the evaluation setting.
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Appendix D.7 reports 3.70 seconds to generate 1,000 Precipitation samples and explains that CrossTF uses only 18 denoising steps. This is useful evidence of practical speed, but ImagenTime also uses 18 steps, while its reported backbone is wider (128 versus 64 base channels). Moreover, CrossTF uses two denoisers within the fusion window and incurs a separate coefficient-optimization cost. Please report matched-backbone and batch-size timing, actual denoiser evaluation counts, and separate training, fusion-optimization, and generation costs so the efficiency claim can be attributed to the proposed design.
Questions for authors
See Weaknesses.
11 comments
Response to Weaknesses 1 (2/2) & Response to Weaknesses 2 (1/2)
(3) Predictive Utility on Unseen Real Data. Although our original protocol follows common practice in the field, we fully agree with the reviewer that holding out real test data provides a more rigorous evaluation. We therefore adopt an 80%/20% train/test split: the generator, including fusion parameter optimization, is trained exclusively on the 80% training set, while the downstream predictor is trained only on synthetic data. The remaining 20% of real sequences are reserved exclusively for testing and are unseen by both the generator and predictor. We also report Train on Real, Test on Real (TRTR) as a reference, where the predictor is trained directly on the 80% real training data under the same split. As shown in Table TR4, CrossTF achieves nearly identical predictive errors under the held-out and original protocols (difference ≤ 0.0008), with performance comparable to TRTR (difference ≤ 0.0002). These results demonstrate that CrossTF's predictive utility does not depend on whether the generator has seen the test data. Details are provided in Appendix K.
Table TR4. Predictive utility under the original and held-out evaluation protocols (MAE ↓). Lower is better.
| Dataset | CrossTF (Original) | CrossTF (80/20 Held-out) | TRTR (Reference, 80/20 Held-out) |
|---|---|---|---|
| Building | 0.0026 | 0.0024 | 0.0024 |
| ECG | 0.0069 | 0.0068 | 0.0066 |
| Electricity | 0.0298 | 0.0303 | 0.0303 |
| Precipitation | 0.0325 | 0.0317 | 0.0318 |
| Temperature | 0.0161 | 0.0158 | 0.0157 |
| Traffic | 0.0198 | 0.0198 | 0.0198 |
| Transportation | 0.0095 | 0.0091 | 0.0090 |
Weakness 2: Robustness of the Cross-View Window
We sincerely thank the reviewer for raising this important question. We first clarify the design idea behind the cross-view fusion window. Rather than optimizing the window separately for each dataset, we prioritize the generality and practical applicability of CrossTF. We therefore adopt a unified fusion window across all datasets, avoiding dataset-specific tuning. This window is not arbitrarily chosen but is grounded in our data-driven analysis: Figures 6 and 7 show that, across all seven datasets, the last six denoising steps are where cross-view discrepancies become stable and extreme fidelity is most sensitive to fusion.
To further validate the robustness of this unified window (σ ≤ 0.35), we conduct two additional experiments: (1) varying the window boundary while fixing the total number of sampling steps to compare the unified window with dataset-specific optimal windows; and (2) varying the total number of sampling steps while keeping the window defined by σ ≤ 0.35 to examine its effectiveness across different sampling configurations. Details are provided in Appendix L.
(1) Window Boundary Ablation. To verify whether the unified window (k = 6) is close to the optimal window on each dataset, we fix the total number of sampling steps to 18 and start the fusion window at the k-th last step (k ∈ {2, 4, 5, 6, 7, 8, 10, 12, 15}), keeping all other settings identical to CrossTF. To eliminate the effect of different numbers of parameters across windows, we optimize a single shared α for each setting. As shown in Table TR5, the improvement in extreme fidelity rises rapidly as k increases from 2 to 6 and largely stabilizes for k ≥ 6. The unified window k = 6 is close to the dataset-specific optimal window on all seven datasets, with a gap of at most 0.4 percentage points. Moreover, under the step-wise fusion of CrossTF, enlarging the window requires solving for more fusion parameters α, which increases the optimization cost without bringing noticeable gains. These results confirm that the unified window serves as a robust and near-optimal default across datasets, without requiring dataset-specific tuning.
Table TR5. Improvement in extreme fidelity over Time-Only under different window starting points k (18 sampling steps, single shared α).
| Dataset | k=2 | k=4 | k=5 | k=6 (Default) | k=7 | k=8 | k=10 | k=12 | k=15 |
|---|---|---|---|---|---|---|---|---|---|
| Precipitation | +0.5% | +10.0% | +13.7% | +14.5% | +14.6% | +14.9% | +14.4% | +14.4% | +14.7% |
| Electricity | +3.6% | +51.4% | +55.3% | +56.4% | +55.8% | +55.9% | +55.9% | +55.3% | +55.6% |
| Temperature | +0.1% | +13.2% | +14.3% | +14.8% | +14.1% | +11.3% | +14.3% | +15.1% | +14.7% |
| Traffic | +0.1% | +1.1% | +1.0% | +1.7% | +0.8% | +0.4% | +0.0% | +0.4% | +0.3% |
| Transportation | −0.4% | +2.2% | +3.8% | +5.6% | +5.8% | +5.4% | +4.8% | +5.6% | +6.0% |
| Building | +1.1% | +10.1% | +12.4% | +13.1% | +13.2% | +12.9% | +12.4% | +12.2% | +12.3% |
| ECG | −0.3% | +2.7% | +5.3% | +5.8% | +5.8% | +5.9% | +5.7% | +5.2% | +5.8% |
Response to Weaknesses 2 (2/2) & Response to Weaknesses 3 (1/2)
(2) Sampling Step Ablation. To examine whether the cross-view benefit persists across different sampling steps, we vary the total number of steps among 12, 18, 32, and 50, while keeping the fusion window defined by σ ≤ 0.35 and all other settings identical to Experiment (1). In Table TR6, each percentage represents the improvement in extreme fidelity of CrossTF over Time-Only at the same sampling steps. Positive values indicate a benefit from cross-view fusion; since the Time-Only baselines differ across step settings, these percentages are not directly comparable across columns. The results show that CrossTF consistently outperforms Time-Only on all seven datasets at 18, 32, and 50 steps, demonstrating that the fusion benefit persists across different sampling steps. At 12 steps, the improvement varies considerably across datasets: it is substantial on Precipitation, Electricity, and Traffic, while the changes on the other datasets are close to zero or negative. Overall, with 18 or more sampling steps, the unified fusion window (σ ≤ 0.35) consistently improves extreme fidelity across all seven datasets.
Table TR6. Extreme fidelity of Time-Only → CrossTF under different numbers of sampling steps (window defined by σ ≤ 0.35, single shared α). Percentages denote the improvement of CrossTF over Time-Only under the same number of steps.
| Dataset | 12 Steps | 18 Steps (Default) | 32 Steps | 50 Steps |
|---|---|---|---|---|
| Precipitation | 0.318 → 0.161 (+49.4%) | 0.111 → 0.095 (+14.5%) | 0.097 → 0.080 (+17.7%) | 0.095 → 0.084 (+11.9%) |
| Electricity | 0.457 → 0.211 (+53.9%) | 0.164 → 0.072 (+56.4%) | 0.165 → 0.066 (+60.1%) | 0.162 → 0.077 (+52.2%) |
| Temperature | 0.242 → 0.242 (−0.2%) | 0.106 → 0.090 (+14.8%) | 0.100 → 0.084 (+16.3%) | 0.121 → 0.104 (+13.7%) |
| Traffic | 0.084 → 0.070 (+16.2%) | 0.028 → 0.028 (+1.7%) | 0.061 → 0.043 (+29.9%) | 0.073 → 0.051 (+30.2%) |
| Transportation | 0.124 → 0.124 (−0.2%) | 0.049 → 0.046 (+5.6%) | 0.063 → 0.061 (+2.7%) | 0.071 → 0.061 (+13.6%) |
| Building | 0.074 → 0.076 (−2.7%) | 0.100 → 0.087 (+13.1%) | 0.126 → 0.122 (+3.3%) | 0.133 → 0.129 (+2.9%) |
| ECG | 0.441 → 0.441 (+0.1%) | 0.141 → 0.133 (+5.8%) | 0.132 → 0.129 (+2.2%) | 0.127 → 0.122 (+3.7%) |
Weakness 3: Choice of EDM and Robustness to Diffusion Backbones
We sincerely thank the reviewer for this insightful comment. We first explain why EDM is well suited to cross-view fusion, then examine whether the cross-view benefit persists with another diffusion backbone through two modifications: (1) replacing Heun with Euler sampling (corresponding to deterministic DDIM-style updates), and (2) replacing EDM with the VP formulation (DDPM-style ε-prediction and variance-preserving noise schedule). We acknowledge that both variants remain within EDM's unified design space rather than representing fundamentally different generative paradigms. Evaluating fundamentally different diffusion architectures would require redesigning and retraining our entire network architecture and pipeline, which is beyond the scope of this rebuttal and left to future work. Details are provided in Appendix M.
(1) Why EDM? We adopt EDM as the base diffusion framework for three reasons:
- Shared Output Space (Preconditioning). EDM's preconditioning (, , ) allows both denoisers to produce clean-sample estimates in the same data space and at consistent scales, enabling the linear fusion in Eq. 5.
- Explicit Noise Parameterization. EDM directly conditions denoisers on the noise level , aligning both views at each denoising step. This allows us to define the fusion window by noise level () rather than step count, and analyze the evolution of cross-view discrepancies (Section 3.2).
- Deterministic Sampling. Given the same initial noise, fused and unfused sampling differ only in the fusion weights , enabling controlled comparisons and optimization. The sampling steps and fusion window can also be adjusted without retraining the denoisers.
Notably, these properties are not unique to EDM. As demonstrated in the following experiments, the cross-view benefit persists under alternative diffusion configurations.
Response to Weaknesses 1 (1/2)
We sincerely thank the reviewer for their recognition and strong support of our work. We are encouraged by their positive assessment of our research direction, well-motivated analyses, clear presentation, and extensive experiments. To further address the reviewer's comments, we have added new analyses and experiments in Appendices J–O (Pages 49–54) of the revised manuscript. We respond to each comment below.
Weakness 1: Train/Test Protocol and Utility on Unseen Real Data
We sincerely thank the reviewer for this valuable suggestion. We agree that predictive utility should be evaluated on real sequences unseen by the generator to properly assess its generalization. We first clarify our evaluation protocol and provide a memorization analysis, followed by new predictive results under an explicit train/test split.
(1) Evaluation Protocol for Unconditional Time-Series Generation. We first clarify the evaluation protocol adopted in our paper. Unlike supervised learning, which typically requires an explicit train/validation/test split, unconditional time-series generation aims to learn the underlying distribution of the training data. In practice, a common evaluation protocol in this field assesses generation fidelity using the same data for both training and evaluation, as adopted by representative methods such as TimeGAN [1] and Diffusion-TS [2]. Moreover, CrossTF and all baselines follow exactly the same data and evaluation protocol, ensuring a fair comparison.
[1] Time-series Generative Adversarial Networks. NeurIPS, 2019.
[2] Diffusion-TS: Interpretable Diffusion for General Time Series Generation. ICLR, 2024.
(2) Predictive Utility Evaluation and Data Memorization. For predictive utility, we adopt the widely used Train on Synthetic, Test on Real (TSTR) protocol, where the downstream predictor is trained exclusively on synthetic data and never directly accesses the real test data during training. Although the generator is trained on the same real data used for testing, this does not necessarily mean that the synthetic data contain leaked information from these samples. To examine this concern, we conduct a new memorization analysis using three metrics: 1 − DCR [3], 1 − NNDR [4], and Copy Rate [5]. The Real Data (Reference) row measures the natural similarity between independent real sequences by comparing each sequence with the others. As shown in Tables TR1–TR3, CrossTF and other advanced generative methods exhibit near-zero copy rates, consistent with the real-data reference. These results suggest that synthetic data contain minimal replication of real test samples, reducing the risk of indirect data leakage to the predictor and supporting the validity of the TSTR evaluation. Details are provided in Appendix J.
[3] Data Synthesis based on Generative Adversarial Networks. VLDB, 2018.
[4] CTAB-GAN: Effective Table Data Synthesizing. ACML, 2021.
[5] Extracting Training Data from Diffusion Models. USENIX Security, 2023.
Table TR1. Memorization evaluation using 1 − DCR across datasets. Lower is better.
Table TR2. Memorization evaluation using 1 − NNDR across datasets. Lower is better.
Table TR3. Copy rate (%) across datasets. Lower is better.