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Under review as a conference paper at ICLR 2027

SCTF: Self-Correcting Time-Frequency Diffusion for Multivariate Time-Series Anomaly Detection

Abstract

Recently, diffusion models have shown considerable promise for multivariate time-series anomaly detection by reconstructing masked observations from the remaining context and using reconstruction errors as anomaly evidence. However, anomalies in the visible context can bias the reconstruction toward abnormal patterns, making the reconstruction appear more similar to the anomalous observations and thereby making the anomalies harder to distinguish. Existing strategies attempt to limit the influence of unreliable conditioning contexts, but such control relies on reliability estimates that may themselves be inaccurate and are often treated as fixed during reconstruction. This reveals a broader bottleneck: effective anomaly reconstruction depends not only on reconstruction capability, but also on whether conditioning reliability can be accurately estimated, controlled, and corrected. To address this bottleneck, we introduce SCTF (Self-Correcting Time-Frequency Diffusion), built on the principle that conditioning reliability should be treated as a dynamic quantity rather than a fixed judgment. SCTF estimates context risks from complementary views, uses them to adaptively reduce the influence of potentially unreliable contexts, and progressively refines the risks using reconstruction feedback, forming a self-correcting loop between reliability estimation and generative reconstruction. Synchronized temporal and frequency diffusion further allows frequency-domain reconstruction to provide auxiliary information for temporal denoising while offering complementary feedback for risk refinement. Extensive experiments on benchmark and real-world datasets demonstrate strong F1 performance against representative state-of-the-art methods.

Primary area:
learning on time series and dynamical systems
Keywords:
multivariate time series, anomaly detection, diffusion models

Reviews

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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_XZtyOpenReview ↗
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Paper summary

This paper proposes SCTF, a Self-Correcting Time-Frequency Diffusion framework for multivariate time-series anomaly detection. The motivation is that anomalous observations in the visible conditioning context can bias diffusion-based reconstruction, making anomalies easier to reconstruct and therefore more difficult to detect.

Critical strengths

(1) The paper identifies a relevant failure mode of conditional diffusion for anomaly reconstruction and proposes a coherent approach.

The observation that anomalous values in the visible context can affect reconstruction is clearly motivated. SCTF addresses this issue at the conditioning stage rather than only increasing reconstruction capacity. The combination of multi-view risk estimation, risk-adaptive corruption, and synchronized temporal-frequency reconstruction forms a consistent pipeline.

(2) The paper provides a broad empirical analysis.

Beyond the main benchmark results, the paper includes ablations of corruption strategies, self-correcting refinement, temporal-frequency coupling, and individual anomaly priors. It also reports risk–ground-truth alignment, hyperparameter sensitivity, three-seed stability, no-point-adjustment results, cross-domain evaluation, and model-efficiency comparisons. These experiments provide useful evidence about the contributions of different components.

Critical weaknesses

(1) The comparison is not based on uniformly reproduced baselines.

A. In Sec. 4.3, Table 1 compares SCTF with existing methods on SMAP, SMD, PSM, MSL, and SWaT under the point-adjustment (PA) protocol. However, the table caption states that baseline results are collected from published studies rather than reproduced using the authors' experimental pipeline. Appendix B.5 further clarifies that the authors use results from the original papers when available and, where applicable, adopt better results reported in subsequent studies.

B. This limitation is relevant because Table 1 provides much of the evidence for SCTF's reported performance advantage, including the highest average F1 score of 96.41 across the five benchmarks. However, Appendix B.2 indicates that the evaluation follows the PA settings of the respective sources rather than a unified experimental pipeline. Although these results share the general PA protocol, they may differ in preprocessing, window construction, data splits, threshold selection, and hyperparameter tuning. These differences make the reported performance gaps harder to interpret.

C. Appendix B.5 also excludes CATCH and CrossAD from Table 1 because their evaluation protocols differ from the adopted PA setting, which further indicates variation across published experimental configurations. Therefore, Table 1 may be better viewed as a comparison with previously reported results rather than as a controlled state-of-the-art comparison. Reproducing several representative baselines, particularly related diffusion-based methods, under the same preprocessing, windowing, thresholding, and tuning procedures would make the comparison more informative.

(2) The experimental design provides limited direct validation of the proposed core mechanism.

A. The cross-domain generalization evaluation in Sec. 4.3 and Table 2 is not entirely independent of target-domain data. According to Appendix B.1 and Table 5, SCTF is trained on STEAD and evaluated on OBST2024, DAS-MedSea, and ShipsEar with fixed model parameters and hyperparameters, without target-domain retraining. However, the detection threshold is calibrated separately for each target dataset using its validation anomaly-score distribution, as specified in Appendix B.4.

Although this unlabeled calibration is reasonable, and Table 2 also reports threshold-independent AUPRC, the setting is more accurately described as fixed-model cross-domain transfer with target-domain unlabeled threshold calibration rather than a strictly target-data-free zero-shot setting. Reporting a source-domain-only threshold or a separate target-data-free setting would make the scope of the generalization claim clearer.

B. The experiments provide only indirect evidence for SCTF's central motivating hypothesis. The Introduction and Fig. 1 argue that anomalous observations in the conditioning context can bias reconstruction toward abnormal patterns, reduce the distinction between normal and anomalous reconstruction errors, and potentially increase missed detections. Sec. 3.4 addresses this issue through risk-adaptive context corruption, where Eq. (5) applies stronger corruption to higher-risk observations to reduce their influence on reconstruction.

C. The current experimental evidence primarily evaluates downstream detection performance. In Sec. 4.4, Table 3 compares No Isolation and Hard Isolation with the risk-adaptive corruption scheme and reports F1 differences on STEAD and PSM. Appendix B.8 and Table 13 further evaluate No Isolation, Oracle Corruption, Random Isolation, Hard Isolation, Fixed Corruption, and different adaptive corruption strengths.

These results indicate that the treatment of conditioning contexts affects detection accuracy, but they do not directly test the relationship illustrated in Fig. 1: whether increasing anomaly contamination in the conditioning context biases reconstruction toward anomalous observations, reduces the anomaly reconstruction-error gap, and consequently increases missed detections.

Questions for authors
  1. Related to Weakness 1: Could the authors reproduce several representative baselines from Table 1 using the same data splits, preprocessing pipeline, input-window configuration, hyperparameter-selection procedure, and thresholding strategy as SCTF? How much of the reported performance advantage remains under a more controlled setting?

  2. Related to Weakness 2: Could the authors provide a more direct evaluation of the hypothesis that anomalous conditioning contexts bias reconstruction toward abnormal observations and reduce anomaly reconstruction errors? For example, if the level of anomaly contamination in the conditioning context is progressively increased while the reconstruction target is held fixed, does the anomaly reconstruction-error gap decrease, and can SCTF mitigate this effect?

1 comment
AuthorsOpenReview ↗

Official Response to Reviewer XZty

We sincerely thank the reviewer for the thorough evaluation and constructive suggestions. We particularly appreciate the concerns regarding baseline comparability, the scope of cross-dataset transfer, and direct validation of our motivating hypothesis. We have revised the manuscript and conducted additional experiments to address these issues.

1. Unified Baseline Reproduction and Fair Comparison (W1, Q1)

Response: We agree that comparisons based on results collected from different publications may be affected by inconsistent experimental settings. To address this concern, we have reproduced all baselines using their publicly available implementations under a unified experimental protocol, rather than relying on previously reported results.

Specifically, all methods use the same training, validation, and test partitions, preprocessing, and evaluation protocol. Hyperparameters are selected using the same validation data and F1 criterion, with comparable tuning efforts. Detection thresholds are calibrated from validation anomaly scores without labels. These changes are documented in Section 4.2.

The updated Table 1 reports the results under this unified setting. SCTF achieves the highest average F1-score across the five benchmarks, although performance varies across individual datasets. These results provide a more controlled basis for comparing SCTF with existing methods, reducing the influence of differences in experimental configurations.

2. Scope of Cross-Dataset Transfer (W2-A)

Response: We agree that target-domain threshold calibration should be distinguished from a strictly target-data-free zero-shot setting.

Our experiments train SCTF on STEAD and transfer the fixed model to ShipsEar, OBST, and DAS-MedSea without target-domain retraining or hyperparameter adjustment. However, the detection threshold is calibrated separately using unlabeled validation anomaly scores from each target dataset. We have clarified this distinction in Section 4.3 and Appendix B.1.

We therefore describe the evaluation as fixed-model cross-dataset transfer with unlabeled target-domain threshold calibration, rather than strictly zero-shot detection.

The expanded Table 2 reports Precision, Recall, F1, and threshold-independent AUPRC under the unified no-PA protocol. SCTF achieves competitive results across the evaluated datasets, while other methods perform better on certain metrics or datasets. These findings provide evidence of transferability within the evaluated seismic and underwater acoustic scenarios, without implying a strictly target-data-free setting.

3. Direct Validation of Anomalous Context Contamination (W2-B/C, Q2)

Response: We appreciate the reviewer's observation that the original ablation studies primarily demonstrated downstream detection improvements without directly validating the mechanism illustrated in Fig. 1.

To address this concern, we have added a controlled experiment in Section 4.5 (Fig. 3) and Appendix B.13 (Table 18). We select anomalous reconstruction targets from 10 STEAD sequences, keeping their values and masking positions fixed while increasing the proportion of anomalous conditioning contexts from 0% to 50% and 100%.

We compare the same pretrained SCTF model under two inference configurations: (1) r=0r=0, which disables risk-adaptive corruption, and (2) Full SCTF, which estimates context risks and applies adaptive corruption. All other reconstruction settings remain unchanged.

The average reconstruction MAE on anomalous targets is summarized below:

Context Contamination0%50%100%
Without Risk Adaptation (r=0r=0)3.122.752.41
Full SCTF3.403.343.30

Without risk adaptation, increasing anomalous context contamination reduces the reconstruction error on anomalous targets, indicating that anomalous contexts can bias reconstruction toward abnormal observations and potentially weaken anomaly evidence. In contrast, Full SCTF maintains relatively stable reconstruction errors, suggesting that risk-adaptive corruption can mitigate this effect.

Fig. 3 further illustrates this trend on a representative anomalous target. These results provide direct experimental evidence for the motivating hypothesis, complementing the downstream detection results.

We sincerely appreciate the reviewer's constructive feedback. The unified baseline comparisons, clarified transfer setting, and direct context-contamination experiment have helped us improve the experimental rigor and presentation of the manuscript. We hope these revisions address the concerns and welcome further discussion!

Reviewer_wLsWOpenReview ↗
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Paper summary

The paper targets reconstruction-based multivariate time-series anomaly detection with diffusion models, and argues that the binding constraint is not reconstruction capacity but conditioning reliability: when the visible context already contains anomalies, the masked-target reconstruction is biased toward abnormal patterns, which flattens the residual and causes missed detections. SCTF operationalizes this as a closed loop. (i) Multi-view context risk: three hand-designed priors — wavelet time-frequency energy (max over channels), smoothed local amplitude (mean over channels), and cross-channel correlation deviation (1 − mean |ρ|) — are z-scored; before any refinement they are averaged and squashed to [0,1]; afterwards a light temporal CNN fuses them into a risk sequence r(t). (ii) Risk-adaptive corruption: the observed context is corrupted with a per-position cumulative coefficient ρ̃_{k,r} = ρ̃_k^{1+r_i}, so high-risk positions contribute less; this is done for masked targets in four mutually exclusive, collectively exhaustive masks. (iii) Synchronized temporal/frequency diffusion: a second denoiser operates on wavelet band aggregates (B = 3 bands, temporal axis preserved), and its clean-state estimate is mapped to the time domain by a 3-layer MLP and blended into the temporal clean-state estimate with a linearly increasing weight γ_k. (iv) Self-correcting refinement: every 10 epochs, the risk is re-fit to a target that mixes the current risk with min-max-normalized temporal and frequency reconstruction errors. Evaluation is on five benchmarks (SMD, MSL, SMAP, PSM, SWaT) under point adjustment (PA), plus a unified no-PA protocol, plus four 3-channel seismic/acoustic datasets for cross-domain transfer.


Update after rebuttal: Concerns partly resolved. However, the scores are maintained since the threshold-free evidence still says the diffusion branch is not the detector. The new Table 13 has conflicting data cross-checked with table 14.

Critical strengths

The problem framing is genuinely useful. "Conditioning reliability as a dynamic, correctable quantity" is a cleaner way to state why context-aware imputation detectors fail on contaminated windows than "limited reconstruction capacity," and it yields a concrete mechanism (per-position, per-step corruption) rather than a loss-term tweak.

The unified no-PA comparison (Table 18) is the strongest evidence in the paper and it favors SCTF by a non-trivial margin: average F1 80.41 vs. 73.09 (ImDiffusion), 69.34 (CATCH), 65.31 (DiffAD), 48.41 (Anomaly Transformer) on PSM/SMD/SWaT, all re-run under one input/window configuration. Presenting this as a first-class result — rather than an appendix — would substantially strengthen the paper.

Table 14's risk–label alignment diagnostic is a good idea: it reports the risk sequence's own P/R/F1/AUPRC against ground truth (labels used only for evaluation), which ties the mechanism to observable behavior rather than to end-task numbers alone.

Critical weaknesses

The "self-correcting" loop is self-referential, and the reported evidence already suggests the diffusion branch is redundant with the risk score at inference. The refinement target (Eq. 16) mixes the current risk with the min-max-normalized reconstruction errors — i.e., the same residual that defines the anomaly score — so the loop trains the risk to predict the detector's own output and then feeds it back into how much context is trusted. Table 14 shows where this leads: risk-vs-ground-truth F1 is 98.19 on STEAD and 98.47 on PSM, numerically indistinguishable from the final detection F1 of 98.17 ± 0.38 and 98.47 ± 0.29. Two consequences are intrinsic to the design rather than to reporting: (a) the claim that synchronized time-frequency diffusion drives detection is unsupported by any comparison where the risk score alone is the detector; (b) there is no argument — contraction, fixed point, or saturation analysis — that the loop does not converge to a self-confirming risk (risk high → context suppressed → residual reproduces the risk), and no diagnostic showing the risk does not saturate. A rebuttal can add the missing baseline, but it cannot supply the missing analysis, and the numbers already in the paper point the wrong way for the stated contribution.

"Frequency-domain diffusion" does not compute what the framing claims. The frequency branch operates on B = 3 non-overlapping band aggregates of a wavelet transform that are deliberately not invertible; a learned 3-layer MLP then projects bands back to the time domain, and that learned projection — not a spectral constraint — enters the temporal clean-state estimate (Eq. 11). The increasing γ_k schedule is justified by coarse-to-fine spectral evolution observed in RGB diffusion, an argument that does not transfer to an aggregated, non-invertible representation. What is implemented is therefore a second denoiser on a coarse multi-scale representation plus a learned fusion, which is a reasonable design but is described in the abstract, introduction and contributions as auxiliary frequency-domain reconstruction with complementary spectral feedback. That mismatch is a matter of claim scope, not of experiment, and cannot be settled by rebuttal; the paper would need to weaken the framing (or replace the branch with an invertible transform).

The cross-domain generalization evidence cannot carry the weight placed on it. All four transfer datasets are 3-channel signals with 10/10/10 entities, 150 k points and anomaly rates of 15.9%–30.2% — far easier than the 25–55-dimensional benchmarks — and the baselines are transferred from STEAD without fine-tuning. Under those conditions SCTF is not uniformly best: on OBST, ImDiffusion attains higher F1 (94.47 vs. 92.79), and on ShipsEar its AUPRC trails two baselines (99.73 vs. 99.93/99.91). The label semantics (earthquake onsets, whale calls, vessel noise) also differ from the "fault" notion of MTS-AD benchmarks, so the reported F1s are not comparable to the standard task. This is a property of the chosen benchmarks and cannot be repaired within the rebuttal window.

The comparison is tuned asymmetrically, so every reported margin is an upper bound. SCTF's hyperparameters are selected on the labeled validation split by validation F1 (Sec. 4.2, App. B.3), with demonstrated sensitivity of 2.5–6.5 F1 points between neighbouring settings (B = 2→3: 96.10→98.39; γ_max = 0.25→0.50: 95.63→98.39; (λ_1, λ_2) = (0.2, 0.5)→(0.5, 0.2): 93.02→98.39; depth 2→4: 91.86→98.39), while baseline numbers are taken at published settings with no stated tuning budget. Since several headline gaps are ≤ 1.5 F1 points, the direction of the comparison is not separable from the tuning asymmetry, and this cannot be undone after the fact. (The detection threshold itself is correctly label-free, δ_d = μ_d + σ_d from validation scores; the model selection is not.)

Questions for authors

What are detection F1/AUPRC when (a) the refined risk r(t) alone and (b) the initial averaged priors alone are used as the anomaly score? Given Table 14's near-identity with the full pipeline, this is the experiment that establishes whether the time-frequency diffusion contributes at inference.

Please specify it precisely: point-wise P/R/F1 with one dataset-level δ_d? How are scores aggregated over the four masks and overlapping windows, and is any smoothing applied? SMD 84.23 and SWaT 76.14 are well above the range usually reported for unadjusted evaluation on these datasets (~60–70); please reconcile — in particular, could the mask assembly plus window overlap partially reproduce PA's segment effect?

Why aggregate wavelet coefficients into three non-invertible bands and learn a projection rather than retain coefficients so that W⁻¹ applies? Please ablate (i) invertible wavelet reconstruction, (ii) a non-wavelet multi-scale auxiliary branch (e.g., strided convolutions) at matched parameter count, and report whether the gain is "frequency" or "an extra denoiser + capacity."

2 comments
AuthorsOpenReview ↗

Official Response to Reviewer wLsW [1/2]

We sincerely thank the reviewer for the detailed and critical assessment. We particularly appreciate the concerns regarding the self-correcting mechanism, the role of frequency-domain diffusion, cross-dataset generalization, baseline fairness, and no-PA evaluation. These comments have helped us clarify the scope of our claims and strengthen the experimental analysis. We address each issue below.

1. Self-Correcting Risk Refinement and the Contribution of Diffusion (W1, Q1)

Response: We appreciate the reviewer's concerns regarding the self-referential nature of risk refinement and the incremental contribution of diffusion inference. To address these issues, we have expanded Appendix B.9 (Tables 13 and 14) to compare initial context risks, refined risks, and Full SCTF Detection.

In the original risk–label alignment analysis, we selected thresholds by maximizing validation F1 to assess the anomaly-discrimination capability of context risks, which measure conditioning reliability rather than directly serve as detection scores. We thank the reviewer for highlighting the importance of a consistent detection-level evaluation. Accordingly, Table 13 now uses the same label-free threshold calibration strategy for Risk-only and Full SCTF Detection, while Table 14 additionally reports validation-F1-selected threshold results.

The F1 results in Table 13 are summarized below:

DatasetInitial Risk (#Ref.=0)Refined Risk (#Ref.=4)Full SCTF (#Ref.=4)
STEAD84.3996.6598.17
PSM79.3397.4098.47

Risk refinement substantially improves the detection capability of the initial risks, while diffusion reconstruction provides a further, relatively modest F1 improvement. We acknowledge that the additional benefit of diffusion inference should be considered alongside its computational cost.

Regarding the potential self-referential behavior, we have added Appendix B.17 (Table 23) to directly examine how context risks change during refinement. Across both datasets, the average risk decreases for normal observations and increases for anomalous observations, while wrong-direction updates occur relatively infrequently. These results indicate that risk refinement improves the distinction between normal and anomalous regions over the evaluated refinement rounds, rather than simply amplifying all risk estimates. The results demonstrate that risk refinement progressively improves the distinction between normal and anomalous observations over successive refinement rounds.

2. Frequency-Domain Representation and Auxiliary Diffusion (W2, Q3)

Response: We thank the reviewer for the careful examination of our frequency-domain design. We have clarified the description of this component to better reflect its actual role.

As described in Section 3.4, SCTF aggregates wavelet coefficients into three frequency bands to obtain a compact multiscale representation. Since this representation is not directly invertible, a learned projection maps the denoised frequency-band features into the temporal space. The frequency branch is intended to provide auxiliary information for temporal reconstruction and risk refinement, rather than perform exact inverse-wavelet reconstruction. The guidance schedule controls the contribution of this auxiliary information during reverse diffusion.

To further evaluate this design, we have added Appendix B.18 (Table 24) comparing SCTF with:

  • DWT/iDWT: An invertible wavelet representation with inverse-wavelet reconstruction.
  • Multiscale CNN: A non-wavelet multiscale auxiliary diffusion branch with approximately matched parameter counts.
DatasetSCTF F1DWT/iDWT F1Multiscale CNN F1
STEAD98.1797.3095.83
PSM98.4797.5296.59

The results show that SCTF performs better than both alternatives under the evaluated settings. These comparisons suggest that the representation used by the auxiliary diffusion branch influences detection performance, rather than the improvement arising merely from adding another denoising branch.

AuthorsOpenReview ↗

Official Response to Reviewer wLsW [2/2]

3. Scope of Cross-Dataset Generalization (W3)

Response: We agree that the evaluated transfer datasets differ substantially from conventional high-dimensional MTS anomaly detection benchmarks, and that the scope of generalization should be stated carefully.

SCTF is trained on STEAD and evaluated on ShipsEar, OBST, and DAS-MedSea without target-domain retraining or hyperparameter adjustment. However, detection thresholds are calibrated using unlabeled target-domain validation scores. We therefore describe this setting as fixed-model cross-dataset transfer with unlabeled threshold calibration, rather than strictly target-data-free zero-shot detection.

The expanded Table 2 reports Precision, Recall, F1, and threshold-independent AUPRC under a unified no-PA protocol. The results are not uniformly favorable to SCTF: ImDiffusion achieves higher F1 on OBST, while other methods achieve higher AUPRC on certain datasets.

We agree that these experiments primarily assess transfer across three-channel seismic and underwater acoustic signals with different event characteristics. They should not be interpreted as evidence of universal transfer to higher-dimensional MTS benchmarks or to every anomaly type. We have clarified this scope in Section 4.3 and Appendix B.1.

4. Baseline Reproduction and Hyperparameter Tuning Fairness (W4)

Response: We agree that using published baseline results alongside validation-tuned SCTF results introduces uncertainty into performance comparisons.

To address this concern, we have reproduced the baselines using their publicly available implementations under a unified experimental protocol, rather than collecting their results from different publications.

All methods use the same data partitions, preprocessing, and evaluation protocol. Hyperparameters are selected using the same labeled validation data and F1 criterion, with comparable tuning efforts. Detection thresholds are subsequently calibrated from validation anomaly scores without labels.

These revisions are documented in Section 4.2 and Appendix B.5. The revised Table 1 reports the results under this controlled setting. We believe this provides a more consistent basis for interpreting performance differences, while recognizing that hyperparameter sensitivity remains an important consideration.

5. No-PA Evaluation and Anomaly-Score Aggregation (Q2)

Response: We thank the reviewer for requesting a precise explanation of the no-PA evaluation procedure, particularly the handling of masking and overlapping windows.

As clarified in Section 3.6 and Appendix B.4, SCTF uses four complementary reconstruction masks, ensuring that each timestamp receives exactly one reconstruction within each window. For overlapping windows, reconstructed values at shared timestamps are averaged before computing point-wise reconstruction errors.

No smoothing or point adjustment is applied to the final anomaly scores. Predictions are obtained using a single dataset-level threshold, τd=μd+σd\tau_d=\mu_d+\sigma_d, calibrated from unlabeled validation anomaly scores and fixed during testing. Precision, Recall, and F1 are computed directly against the ground-truth labels at each timestamp.

To further examine the relatively high no-PA results, we have added experiments using the official training and test splits of PSM, SMD, and SWaT in Appendix B.14 (Table 20). The results are noticeably lower than those obtained under our customized anomaly-contaminated partitions, indicating that dataset partitioning can substantially influence no-PA evaluation results. These additional experiments provide a clearer assessment of SCTF under the conventional benchmark setting.

We sincerely appreciate the reviewer's rigorous and constructive feedback. The additional comparisons, risk-refinement diagnostics, frequency-branch ablations, and protocol clarifications have helped us better distinguish the supported findings from the remaining limitations. We hope these revisions address the concerns and welcome further discussion!

Reviewer_siXJOpenReview ↗
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3(+1)
Confidence
3
Informativeness
2
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Paper summary

This paper proposes SCTF, which estimates context risks from time-frequency energy, local amplitude, and cross-channel correlation, then uses these risks to control conditional corruption. Complementary masks and coupled temporal/frequency diffusion branches reconstruct the sequence. During training, reconstruction errors periodically refine a risk estimator, which remains fixed at inference.

Critical strengths
  1. The method provides a coherent response to unreliable conditioning. Risk estimates directly control context corruption, while reconstruction feedback updates the estimator. Oracle-risk, isolation, corruption, refinement, and time-frequency ablations provide substantive evidence about the individual mechanisms.

  2. Table 18 reports no-PA results with variability on PSM, SMD, and SWaT, including an average F1 of approximately 80.41 versus 73.09 for the listed ImDiffusion comparison. Risk–label alignment and transfer with a fixed source-trained model provide additional evidence, while permitting target-domain unlabeled threshold calibration.

Critical weaknesses
  1. In Table 14’s default setting, risk–label AUPRC is 99.65/98.52 on STEAD/PSM, while final detection AUPRC is 99.37/96.02. These values require protocol clarification before being treated as a direct comparison, but they make risk-only detection an essential control. This paper needs to distinguish the benefit of diffusion-assisted training from the benefit of running diffusion at inference to justify the complete deployment pipeline.

  2. Wavelet features are computed before temporal masking, so observed coefficients may contain information from masked target timestamps. This is a potential target-information crossover that requires clarification or a controlled experiment. Separately, hyperparameters are selected using labeled validation F1, while the reported validation sizes appear to come from conventional training splits. If those splits are normal-only, the source of anomalous validation examples is unclear.

Questions for authors
  1. Are Table 14’s risk and detection columns evaluated on the same held-out timestamps with comparable AUPRC aggregation? Under the detector’s exact protocol, how does the final risk score alone perform?

  2. Does the implementation transform the complete sequence before masking? If so, how are observed wavelet coefficients that depend on masked target values excluded or otherwise accounted for?

  3. What are the provenance and anomaly-label composition of the validation splits used for F1-based selection? Do the baselines use the same label budget and selection rule? Please distinguish this from unlabeled threshold calibration.

5 comments
AuthorsOpenReview ↗

Official Response to Reviewer siXJ

We sincerely thank the reviewer for the careful evaluation and constructive feedback. Your comments have helped us clarify our methodology and strengthen the experimental validation. We address each concern below.

1. Risk-only Detection and the Contribution of Diffusion Inference (W1, Q1)

Response: We agree that a direct risk-only comparison is essential. We have revised Appendix B.9 (Tables 13 and 14) to compare Risk-only Detection, which directly uses refined context risks without diffusion inference, with Full SCTF Detection, which uses diffusion reconstruction errors. Both follow identical evaluation protocols, held-out timestamps, and score aggregation (no-PA for STEAD; PA for PSM).

In the original risk–label alignment analysis, we maximized validation F1 to assess the anomaly-discrimination capability of context risks, which measure conditioning reliability rather than serve as final detection scores. This allowed us to examine risk–label alignment independently of a particular threshold calibration rule. We thank the reviewer for highlighting this distinction. Table 13 now compares both detectors using the same label-free threshold strategy, while Table 14 additionally reports validation-F1-selected threshold results.

Table 13 reports:

DatasetRisk-only F1Full SCTF F1Risk-only AUPRCFull SCTF AUPRC
STEAD96.6598.1799.6599.37
PSM97.4098.4798.5296.02

Full SCTF improves F1 by 1.52 and 1.07 percentage points, respectively, although Risk-only achieves higher AUPRC. We appreciate the reviewer's observation that the incremental benefit of diffusion inference is limited. These modest F1 gains come at the additional cost of diffusion sampling and may not always justify that cost. Risk-only therefore offers a computationally lighter alternative, while Full SCTF may be preferable when higher F1 is prioritized.

2. Potential Target-Information Crossover in Wavelet Processing (W2, Q2)

Response: We agree that applying CWT before masking may introduce target-information crossover. We therefore added a controlled comparison in Appendix B.16 (Table 22):

  • CWTMask: CWT before temporal masking.
  • MaskCWT: Masking before CWT, with CWT applied independently to contiguous unmasked segments to exclude masked target information.

We use four complementary 25% block masks to preserve contiguous observed segments and avoid additional preprocessing required by fragmented random masks, such as interpolation or segment concatenation.

DatasetCWTMask F1MaskCWT F1CWTMask AUPRCMaskCWT AUPRC
STEAD95.6995.5393.1893.04
PSM95.2894.5693.1594.54

The comparable results suggest that potential information crossover has a limited impact under the evaluated block-masking setting.

3. Validation Data Provenance, Label Usage, and Fair Model Selection (W2, Q3)

Response: We thank the reviewer for prompting us to clarify our data partitioning and label usage. We have revised Appendix B.1 and Section 4.2.

Standard benchmarks typically use normal-only training data, with validation sets often drawn from the same partition. However, real-world training and validation data may contain undetected anomalies. To investigate this setting, we redistribute fixed-length, non-overlapping temporal segments into mutually disjoint training, validation, and test sets, preserving temporal order within segments. Partition sizes are kept as close as possible to the original benchmarks, while training and validation may contain anomalies. Dataset sizes and anomaly proportions are reported in Appendix B.1 (Table 4).

We clarify the three stages:

  • Training: No anomaly labels are used to optimize model parameters.
  • Hyperparameter selection: SCTF and all baselines use the same labeled validation data, F1 criterion, and comparable tuning efforts.
  • Threshold calibration: The threshold τd=μd+σd\tau_d=\mu_d+\sigma_d is computed from validation scores without labels and fixed during testing.

These revisions clarify the distinction between label-based model selection and label-free threshold calibration.

We sincerely appreciate the reviewer's constructive suggestions and hope these additional experiments and clarifications address the concerns. We welcome further discussion!

Thanks for the clarifications and the additional experiments. Some of my concerns remain, so I’m keeping my rating unchanged for now:

  1. CWT comparative experiments employed ''block masks'', whereas the primary experiments utilized ''random masks''. I think validation under the original experimental setup is warranted.

  2. Regarding the results for the official split in Table 20: given that the training data consists exclusively of normal samples, where do the labels used for hyperparameter tuning (based on the F1 score) originate?

Furthermore, upon closer inspection, I have questions regarding several experimental details:

  1. In Table 11, the results for SCTF on the SMD dataset are: P = 91.77 ± 0.48, R = 96.50 ± 0.33, and F1 = 94.08 ± 0.44. If the F1 score was calculated individually for each run, the reported degree of variation seems inconsistent with that of P and R. Similar issues arise in Table 20. Are these metrics aggregated differently? It would be helpful if you could share the per-run results or code to help assess reproducibility.

  2. Under the official split, the average F1-score (w/o Point Adjustment) drops from 80.41 to 58.20. Please explain how the data segments were re-partitioned. Specifically, is it possible for different portions of the same anomalous event to be assigned to different data splits? And were the data splits kept consistent across the three experimental runs?

If these issues can be clearly explained, I would be willing to increase the score.

AuthorsOpenReview ↗

Official Response to Reviewer siXJ

We sincerely thank the reviewer for the careful follow-up and constructive comments. We appreciate the opportunity to further clarify our experimental procedures and improve the transparency and reproducibility of our results. We address the four points below.


1. CWT Comparison Under the Original Random Masking Setting (Comment 1)

Response: We agree that block-mask experiments alone are insufficient to evaluate the original setting. We have therefore extended the comparison to four complementary 25% random masks, consistent with the original SCTF configuration.

In addition to SCTF, which applies CWT before masking, we evaluate two mask-before-CWT variants: Zero-MaskCWT and Linear-MaskCWT. These variants first mask the temporal input, fill the missing values using zeros or linear interpolation from visible observations, apply CWT, and then reapply the same frequency-domain mask.

The block-mask variants achieve comparable performance, whereas the mask-before-CWT variants show lower performance under random masking. However, this degradation cannot be attributed solely to information leakage, since missing-value filling may also introduce spectral distortion. We have clarified this limitation and restricted our conclusions accordingly.

Manuscript revisions: Appendix B.16.


2. Origin of Validation Labels Under the Official Dataset Splits (Comment 2)

Response: Under the official dataset splits, the validation set contains only normal observations. We select hyperparameters by maximizing the validation F1-score for the normal class. Since all validation observations are normal, incorrectly classifying them as anomalous reduces the F1-score. We have clarified this validation procedure in the revised manuscript.

Manuscript revisions: Appendix B.14.


3. Statistical Consistency and Per-Run Results (Experimental Detail 1)

Response: We sincerely thank the reviewer for carefully examining our experimental results and identifying these inconsistencies. After reviewing our statistical analysis code, we found that the standard deviations were mistakenly calculated using the metrics of all segments across the three random seeds, rather than the three seed-level metrics. We had originally collected segment-level statistics to investigate the influence of data partitioning on detection performance, but these values were inadvertently used when reporting standard deviations. The reported means were correctly calculated from the three independent runs, and the inconsistency only affected the standard deviations.

We have corrected the statistical code, recomputed the affected results, and updated the corresponding tables in the revised manuscript. For transparency and reproducibility, we provide the original and corrected statistical code, together with the individual P/R/F1 results from all three seeds for Tables 1, 2, 11, 19, and 20.

Manuscript revisions: Appendix B.6 and Appendix B.14. The statistical code and complete three-seed results are provided in the supplementary materials.


4. Data Re-Partitioning, Event Overlap, and Consistency Across Runs (Experimental Detail 2)

Response: Our customized partitioning strategy aims to simulate more realistic conditions in which both training and validation sets may contain anomalous observations. Specifically, we divide the original time series into fixed-length, non-overlapping segments, randomly shuffle and redistribute them while approximately preserving the original training, validation, and test set sizes.

We acknowledge that different portions of the same anomalous event may be assigned to different partitions, meaning that anomalous patterns in the test set may also be observed during training. We recognize that this potential overlap may lead to optimistic performance estimates.

Regarding consistency across runs, different random seeds produce different data partitions, but all runs follow the same partitioning procedure and preserve the predefined dataset sizes. Importantly, all compared methods use identical partitions under the same seed to ensure fair comparisons.

Manuscript revisions: Appendix B.1 and Appendix B.14.


We sincerely thank the reviewer again for the detailed and constructive feedback. These comments have helped us clarify the evaluation protocols, resolve the statistical inconsistencies, and improve the transparency of our experiments. All corresponding changes in the revised manuscript have been highlighted in blue for ease of reference. We hope these revisions adequately address the remaining concerns, and we welcome further discussion!

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Summary of Responses and Major Revisions

Summary of Revisions and Additional Experiments

We sincerely thank all reviewers for their careful evaluations and constructive feedback. In response to the concerns raised across the three reviews, we have conducted additional experiments and substantially revised the manuscript. The major improvements are summarized below.

1. Reproduction of Baselines Under a Unified Evaluation Protocol

We re-evaluated multiple representative baselines using their publicly available implementations under a unified point-adjustment (PA) protocol, rather than selecting the best reported results from previous publications. This provides a more consistent and fair comparison.

2. Investigation of CWT and Masking Order

To address concerns about potential information leakage from applying CWT before masking, we conducted additional experiments under both block and the original random masking settings. The results show that mask-before-CWT alternatives perform worse under random masking. However, we clarify that this degradation may arise from both reduced information crossover and spectral distortion, rather than information leakage alone.

3. Necessity of Diffusion During Inference

We introduced a direct comparison between Risk-only Detection and Full SCTF Detection. Although the risk estimates alone provide strong anomaly detection performance, diffusion reconstruction further improves F1 by 1.52 percentage points on STEAD and 1.07 percentage points on PSM. We also clarified the corresponding AUPRC trade-offs.

4. Clarification of Experimental Settings and Results

We clarified the dataset partitioning, validation procedures, evaluation protocols, and baseline configurations, and added experiments using official dataset splits. We also refined several conclusions to better reflect the experimental evidence. Following a careful review of our statistical code, we corrected the reported standard deviations and disclosed the individual results from three random seeds.

5. Validation of Self-Correcting Risk Refinement

We added experiments examining risk changes before and after refinement. The results show that self-correcting refinement generally decreases risk estimates for normal observations and increases them for anomalous observations, while incorrect-direction updates remain relatively infrequent. These findings provide direct empirical support for the effectiveness of the refinement process.

6. Additional Experiments Supporting the Motivation

We conducted controlled context-contamination experiments to investigate whether anomalous contexts can facilitate the reconstruction of anomalous targets. The results show that increasing anomalous context contamination reduces the reconstruction error without risk adaptation, whereas SCTF maintains relatively stable reconstruction errors. This provides additional evidence for the motivation behind reliability-aware context corruption.


We sincerely appreciate the reviewers' valuable suggestions, which have helped us strengthen the experimental evidence, clarify important methodological concerns, and improve the reliability of our evaluation. We have addressed the reviewers' questions individually in our detailed responses, with the corresponding manuscript revisions highlighted in blue. We hope these additional experiments and clarifications adequately resolve the concerns raised during the review process!

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