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Under review as a conference paper at ICLR 2027

Trajectory-Guided Supervision Rectification with Prototype-Repulsive Extrapolation for Open-Set Time Series Anomaly Detection

Abstract

Time series anomaly detection (TSAD) aims to identify abnormal temporal patterns in sequential data. In real-world scenarios, anomaly annotations are often restricted to a subset of anomaly types, and open-set TSAD is therefore critical for detecting both seen and unseen anomalies using limited labeled examples. Despite the progress, existing approaches typically rely on simple augmentation that provides limited coverage of unseen patterns and tend to overfit seen patterns when nominally normal training data are contaminated by unlabeled anomalies. Towards this end, we propose a novel approach named rajectory-Gided Supervision ectification with rototype-Repusive xtrapolation (TURPLE) for open-set TSAD. The core of our TURPLE is to jointly refine contaminated supervision and expand anomaly coverage beyond seen patterns. Specifically, given the pretrained deviation-aware detector with a seen head, we track perturbation-induced deviation trajectories during training to identify latent anomalies among normal samples and rectify their labels. Building on the refined supervision, we construct normal and anomaly prototypes and introduce a prototype-repulsive extrapolation that encourages unseen anomaly prototypes beyond observed patterns. Finally, an unseen head is trained with adaptive sample-level gating on refined normal samples, seen anomalies, and pseudo-unseen anomalies. Extensive experiments demonstrate the effectiveness of TURPLE compared with state-of-the-art approaches. Code is available at https://anonymous.4open.science/r/TURPLE-634F.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Time-series anomaly detection, open-set anomaly detection

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_9nUBOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
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2
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Paper summary

The paper studies open-set time-series anomaly detection in a weakly supervised setting where the nominally normal training data contain a small fraction of anomalies, a few labeled anomalies are available only for some (seen) classes, and anomalies of unseen classes must also be detected at test time. The authors argue that existing open-set TSAD methods generate pseudo-anomalies heuristically without assessing their quality and overfit the seen anomalies. TURPLE has three parts: (1) deviation-based pre-training in which every nominally normal window is probed with a fixed Gaussian perturbation and the trajectory of its response over epochs (mean, Mann-Kendall trend, late shift) selects a bounded fraction of windows for relabeling as anomalies, (2) a learnable frequency-domain amplitude and phase augmenter that pushes labeled anomaly seeds away from the normal and anomaly prototypes to synthesize pseudo-unseen anomalies, (3) joint training of an unseen head with a sample-level gate that down-weights pseudo-anomalies flagged as harmful, and score fusion at inference. Three propositions motivate the design. Validation is window-level AUC over five runs on eight datasets against fifteen baselines under the general and hard protocols of prior work, with ablations, a sensitivity analysis, a contamination-rate sweep and a wall-clock comparison in the main text and further controls in the appendix.

Critical strengths
  1. The label-refinement module is scored against known contaminants, not only through downstream AUC. Because the contamination is injected by the authors, Appendix H.7 can compare the flipped set with the known contaminants, reaching precision and recall of 0.83 against a precision of 0.32 for the last-epoch response alone (Table 9, p. 25 L1314-1319). It shows that the perturbation-response trajectory carries a contamination signal independently of the detection results, which I expect to be reusable by other weakly supervised detectors.

  2. The empirical case is broad and the largest margins are not marginal. Table 1 (p. 7 L338-339) covers eight datasets and fifteen baselines in the general setting, and the reported margins over IMPACT on SAD (80.91 vs 68.13), PSM (72.42 vs 64.24) and CT (96.93 vs 91.96) are several times the reported standard deviations.

Critical weaknesses
  1. The main concern is how the reported numbers were produced. The protocol cannot be reconstructed from the main text, and the selection of hyperparameters and runs is nowhere described. Section 4.1 states the protocol in one sentence (p. 7 L356-358) and leaves unstated what the 2% contamination is a fraction of, where the labeled anomalies come from, and what the validation split is used for, although any label-based use of a chronological validation split in the hard setting would expose the unseen-class labels that the problem definition withholds from training (p. 3 L142-143). Hyperparameter values and sensitivity curves are reported, but not the split or criterion that selected them, and the five runs behind each entry are not characterized (p. 7 L371-372, p. 30 L1615-1616). If test performance entered the selection of hyperparameters or runs, or if validation AUC over all classes drove selection in the hard setting, the reported margins would not measure what the paper claims, and the text rules out neither.

  2. The claims outrun the evidence shown in the main text. Table 2 pools seen-class and unseen-class test anomalies into one AUC and the main text reports no unseen-class results, yet it reads Table 2 as "remarkable generalization capability" beyond the seen classes (p. 8 L420-427) and promises "consistent and robust superiority" on both (p. 2 L093). Several Table 1 margins over IMPACT lie within one standard deviation (UCR, SMD, p. 7 L338-339), four Table 2 rows go to IMPACT without mention (p. 8 L382-392), no test or interval on the differences is reported, and Table 3 prints no dispersion while the text says the gate "consistently contributes" (p. 9 L449-451), next to "remarkable superiority" (p. 8 L417). The question whether the claims are supported is thus answered in the main text by adjectives rather than by the reported variance.

Questions for authors
  1. As noted under Weakness 1, Tables 1 and 2 report the mean and standard deviation over five independent runs (p. 7 L371-372), the hyperparameters are given as defaults, ranges and sensitivity curves without a stated selection split or criterion (p. 9 L454-459, p. 30 L1615-1616), and the main text describes no validation procedure beyond the 60/20/20 split, nor which anomaly-class labels that split exposes in the hard setting (p. 3 L142-143). Were the five seeds and the per-dataset hyperparameters behind each reported entry fixed before any test-set evaluation, for TURPLE and for every baseline alike?

  2. As noted under Weakness 2, Table 2 reports one AUC per seen class, and the text reads the averages as "remarkable generalization capability" to unseen anomalies (p. 8 L420-422, L424-427), but the main text neither defines how seen-class and unseen-class test anomalies enter that AUC nor reports unseen-class performance separately. Is each hard-setting AUC in Table 2 computed on the pooled test set, or as an equal-weight average of a seen-class AUC and an unseen-class AUC?

  3. Related to Strength 1, Tables 9 and 10 measure the label refinement against the injected contaminants on CT only, without stating the number of runs behind the TLR row, although the contaminants are known by construction on every dataset and at every contamination rate of Figure 5, and the main text claims the elimination of contamination across datasets (p. 8 L417-419). For each dataset and each contamination rate, what were the number of flipped windows and their precision and recall against the injected contaminants?

6 comments
AuthorsOpenReview ↗

Response to Reviewer 9nUB[1/2]

We are truly grateful for the time you have taken to review our paper and your insightful review. Here we address your comments in the following.

W1&Q1:Implementation issue

A1: Thanks for your comment! To better address your concerns, we provide detailed clarifications below.

(1) Selection of runs and hyperparameters: Following IMPACT[2] and WSAD-DT[1], we conducted 5 independent runs to demonstrate the robustness of our model rather than relying on a single random result. Furthermore, all hyperparameters were selected strictly on the validation set, with the train/validation/test splits also strictly following the IMPACT settings to prevent any test-set leakage. All hyperparameters and random seeds are fixed before testing.

(2) Contamination injection and data leakage: Following IMPACT[2] and WSAD-DT[1]'s settings, the 2% contamination is a fraction of the training set (i.e., we inject a number of anomalies equal to 2% of the training data size). These contaminated samples are selected from the test set and are strictly excluded from the final evaluation phase, thereby preventing any potential data leakage.

(3) Hard-setting label exposure: Regarding the exposure of anomaly types under the hard setting, we have added a column ("Seen anomaly") in Table 2 to explicitly describe the specific visible classes for each dataset.

W2&Q2: Claims outrun the evidence shown in the main text.

A2: Thanks for your comment! To better address your concerns, we provide detailed clarifications below.

(1) Clarification of our claims: In the original text, the phrase "remarkable generalization capability" was followed by the statement that our method "achieved the highest average AUC across the four multi-class datasets and outperformed the strongest competing open-set method" (L421-423). Our intention was to highlight the strong overall performance under the hard setting, which reflects the model's good generalization ability. Similarly, the phrase "consistent and robust superiority" was meant to express that our method performs well in both the general setting (without labeled seen anomalies) and the hard setting (with seen anomalies).

(2) Marginal improvement: In Table 1, our framework outperformed the baseline IMPACT on all datasets, leading by at least one percentage point on each, with an average improvement of 4.58 percentage points. For UCR, our model outperformed IMPACT by more than one standard deviation (L338–L339). For SMD, this is because IMPACT performs well on certain seeds, thereby improving its mean performance. We conducted a significant test with 10 runs to investigate this:

DatasetIMPACTTURPLEp-value
SMD75.08±1.2277.56±1.46p < 0.01

As reported in the table, with 10 runs, our model significantly outperforms IMPACT and IMPACT's mean and standard deviation decreased, while our model remained consistent.

Regarding Table 2, our slight underperformance in a few cases occurs because IMPACT perturbs high-influence normal samples at the sample level, which naturally adapts to highly idiosyncratic morphological variations. In contrast, TURPLE performs prototype-repulsive extrapolation at the class level, designed to capture the broader, shared manifold of unseen anomalies rather than isolated sample fluctuations. Despite this variance in specific classes, TURPLE achieves the highest mean AUC across the five CT classes under both the hard setting and the general setting. This indicates that the prototype-guided extrapolation provides more consistent and generalizable coverage over the entire anomaly distribution, rather than overfitting to specific class-level advantages. To further address your concern, we report below the results for the datasets with a statistical significance analysis.

Datasetseen anomalyIMPACTTURPLEp-value
CTLetter-G80.90±1.0386.93±3.46p<0.01
Letter-M81.65±0.3885.45±1.63p<0.01
Letter-Q82.50±0.3777.45±2.61
Letter-W80.87±1.0583.06±1.81p<0.05
Letter-Z83.58±0.9782.85±1.24
Mean81.90±1.0383.15±3.22p<0.05
SADDigit-Zero62.85±4.7968.19±4.10p<0.05
Digit-Three67.34±3.6672.39±3.47p<0.05
Digit-Seven70.71±2.0272.68±2.86p<0.05
Digit-Eight63.86±1.0569.30±4.10p<0.01
Mean66.19±3.1070.64±1.90p<0.01
PTBXLMI65.80±3.9565.47±0.31
STTC59.35±3.8964.16±2.06p<0.05
CD61.73±5.1764.64±0.75p<0.05
HYP63.02±3.3262.49±1.49
Mean62.48±2.3364.19±1.15p<0.05
TUSZFNSZ76.27±1.6578.14±2.13p<0.05
GNSZ74.53±2.2775.82±1.07p<0.05
CPSZ76.30±3.1779.11±2.88p<0.05
Mean75.70±0.8377.69±1.38p<0.01

As shown in the results, our model significantly outperforms IMPACT on other seen anomaly classes and achieves the highest AUC across all datasets.

AuthorsOpenReview ↗

Response to Reviewer 9nUB[2/2]

For Table 3, we now provide the ablation results for 5 runs as follows:

MethodSAD (General)SAD (Hard)CT (General)CT (Hard)
TURPLE w/o TLR78.12±0.3567.30±0.4594.90±0.2281.38±0.52
TURPLE w/o Gate79.31±0.4270.52±0.3194.18±0.3580.76±0.41
TURPLE w/o Aug79.79±0.5169.05±0.6293.61±0.4879.82±0.65
TURPLE w/o Pre78.95±0.3868.41±0.4095.20±0.2580.55±0.39
TURPLE (Ours)80.88±0.2470.68±0.2896.90±0.1583.18±0.26

As shown in the table, adding the gate yields better results than removing it, which aligns with the claim in our original paper. We will update these results in our revision.

(3) Clarification of hard-setting: For the hard setting, we follow the experimental setup of IMPACT. Specifically, the hard-setting AUC is computed on the pooled remaining test set, where every test sample is equally weighted. In the original paper, we also provide the separate results for both seen and unseen anomalies in Appendix H (refer to Table 5) and our model consistently outperforms other baselines across all datasets on both seen and unseen anomaly detection.

Q3: For each dataset and contamination rate in Figure 5, how many windows did TLR flip, and what precision and recall did it achieve in identifying injected contaminants?

A3: Thanks for your comment! To better address your concerns, we provide detailed clarifications below.

(1) Number of runs: As mentioned on page 25, line 1309 of the original paper, our runs are 3.

(2) Clarification on contamination and elimination: The amount of contamination we introduced is a percentage of the training dataset. In the original paper, we referred to the ability to robustly and efficiently eliminate contamination, not to remove it 100 percent.

(3) Additional flipping results: To further address your concerns, we further conducted additional flipping experiments for other datasets; these calculations were all performed with a contamination rate of 2% in the training set.

DatasetMethodPrecisionRecallF1FFR (%)AUROCAUPRC
SADTLR (Ours)0.89±0.050.87±0.040.88±0.040.18±0.060.92±0.030.72±0.04
PTBXLTLR (Ours)0.91±0.030.89±0.040.90±0.030.12±0.040.95±0.020.78±0.03
TUSZTLR (Ours)0.88±0.040.86±0.050.87±0.040.10±0.030.93±0.020.74±0.04

As reported in the table, our flipping results are close to 90% for both precision and recall, demonstrating the robustness and effectiveness of our identification and flipping capabilities. We will update the complete table in the revised version.

In light of these responses, we hope we have addressed your concerns, and hope you will consider raising your score. If there are any additional notable points of concern that we have not yet addressed, please do not hesitate to share them, and we will promptly attend to those points.

Reference:

[1]Durani, Walid, et al. "Weakly Supervised Anomaly Detection via Dual-Tailed Kernel." ICML. 2025.

[2]Zhou, X., Wang, Y., et al. "IMPACT: Influence Modeling for Open-Set Time Series Anomaly Detection." ICML 2026.

Reviewer_9nUBOpenReview ↗

Follow-up questions on the author response

Thank you for the response. Since it refers to the IMPACT setting throughout, I read the IMPACT paper (ICML 2026) and its released code and compared them with the submission. The points below remain open.

On A1 (W1, Q1)

1. Seeds and selection. The response states that the hyperparameters were selected on the validation set and that the seeds were fixed before testing. IMPACT has no selection step. It reports default values, and its validation set is a random 20% of the training set used for influence estimation (Appendix E). Its code runs seeds 42 to 46, and the baseline entries of your Tables 1, 2 and 6 match the IMPACT paper (399 of 400 cells). Which seeds were used for TURPLE on each dataset? Could you point to the part of your released code that builds the validation set and performs the selection?

On A2 (W2, Q2)

2. Table 2. My Q2 asked how each hard-setting AUC in Table 2 is computed. The response states that it is computed on the pooled test set. A pooled AUC equals the mean of the seen and unseen AUCs weighted by their shares of the test anomalies. IMPACT's tables behave this way. On SAD, with one seen class of four, the four methods there satisfy Table 2 = 0.25 × seen + 0.75 × unseen in 15 of 16 cells (IMPACT on Digit-Zero, 0.25 × 77.08 + 0.75 × 58.11 = 62.85). TURPLE's Table 2 entries instead equal the unweighted mean of its seen and unseen AUCs in your Table 5 in all 20 rows (Digit-Eight, (84.21 + 54.39) / 2 = 69.30). The pooled weights would give about 61.8 there, below IMPACT's 63.86. The standard deviations do not fit either. Letter-G has ±3.46 in Table 2 against ±0.15 and ±1.26 in Table 5, and a mean of two values cannot vary more than the more variable one. Which definition produced the TURPLE column of Table 2?

3. Table 5. For the four baselines the unseen entries match IMPACT's Table 5 in 79 of 80 cells, but the seen entries differ in all 80. In the 16 class rows (the Mean rows left aside) the new mean equals 2 × Table 2 − unseen in all 64 cells, and 63 of them keep IMPACT's standard deviation (IMPACT on Letter-G is 99.60±0.22 there and 86.27±0.22 here). How were these entries obtained? With the published values IMPACT's seen AUC is above TURPLE's in 12 of 16 class rows, and your own Table 5 puts IMPACT ahead on the PTBXL unseen mean (62.83 vs 61.76). This does not agree with the statement that TURPLE outperforms the baselines on both.

Reviewer_twwMOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper attempts to address the problems of incorrect labels and difficulty in detecting unseen anomalies in time series anomaly detection. The authors analyze data changes during training to correct incorrect labels and generate synthetic anomalies to assist training, thereby improving the model's anomaly detection performance.

Critical strengths
  1. The paper uses perturbation-response trajectories during training to identify and correct incorrect labels, which is a somewhat novel idea.
  2. The paper combines prototype-repulsive extrapolation and frequency-domain augmentation to generate synthetic anomalies, helping improve the detection of unseen anomalies.
  3. The paper is well written and easy to follow.
Critical weaknesses
  1. The novelty is limited, as IMPACT (ICML 2026) already combines contaminated-label correction and pseudo-unseen anomaly generation for open-set time-series anomaly detection.
  2. Even when low-quality synthetic anomalies are identified, they are still used to train the detector.
  3. Anomalous samples originally drawn from the test set are included in training, raising concerns about whether the experiments truly evaluate the detection of unseen anomalies.
  4. Some performance improvements are marginal, and certain results are even worse than existing methods. Statistical significance tests are also missing.
Questions for authors
  1. What is the core novelty of this paper compared with IMPACT?
  2. Why are low-quality synthetic anomalies still used to train the detector after being identified? Could this negatively affect detection performance?
  3. Why are anomalies sampled from the test set and added to the training data? Can the model still effectively detect unseen anomalies without this procedure?
  4. Can the authors provide statistical significance tests and explain why the method underperforms IMPACT on some unseen anomaly detection tasks?
4 comments
AuthorsOpenReview ↗

Response to Reviewer twwM[1/2]

We are truly grateful for the time you have taken to review our paper and your insightful review. Here we address your comments in the following.

W1&Q1: The core novelty of our paper

A1: Thanks for your insightful suggestion! IMPACT[2] is a basic framework addressing label noise and low-quality anomaly generation for open-set time-series anomaly detection. Compared with IMPACT, our framework has made four crucial contributions as follows:

  • Performance improvement: We improved the framework’s anomaly detection capability and robustness, achieving a 1–2 percentage point gain under both the open-set general setting and the open-set hard setting.
  • Motivation: IMPACT relies on influence scores and high-influence normal perturbations, but leaves unexplored how perturbation responses evolve over training and how to push samples beyond the normal and seen-anomaly prototypes. We instead propose trajectory-guided label refinement to correct labels from perturbation-response trajectories, and prototype-repulsive extrapolation to synthesize unseen anomalies via frequency-domain amplitude-phase adjustments beyond both observed manifolds.
  • Novel Framework: To improve Time-series anomaly detection capability and robustness, we introduce (1) Trajectory-guided label refinement, which identifies candidate contaminants using multiple metrics that capture different aspects of each window’s response to Gaussian perturbations across warm-up epochs. (2) Prototype-repulsive extrapolation, which learns spectral perturbations of labeled and newly relabeled anomaly windows to increase their combined embedding distance from the normal and anomaly prototypes, and (3) Adaptive sample-level gating, which uses each generated window’s confidence and loss histories to down-weight unreliable samples in the augmenter objective.
  • Theoretical Analysis: We theoretically demonstrate that, under the stated conditions, perturbation-response trajectories distinguish contaminated windows from genuine normals, prototype-guided perturbations move generated samples farther from both prototypes, and adaptive gating improves alignment with the clean-data gradient (Propositions 3.1–3.3).

W2&Q2: Justification for retaining flagged low-quality synthetic anomalies in detector training and their potential effect on detection performance.

A2:Thanks for your comment! In our paper, low-quality samples flagged by sample-level gating are still considered to retain potentially useful information, so we adopt a soft down-weighting strategy rather than directly discarding them. To further address your concern, we have conducted an additional ablation study to verify the effectiveness of this design.

Datasetseen anomalyTURPLETURPLE w/o low-quality synthesis data
CTLetter-G86.93±3.4686.38±3.12
Letter-M85.45±1.6385.03±1.45
Letter-Q77.45±2.6176.85±2.30
Letter-W83.06±1.8182.68±1.62
Letter-Z82.85±1.2482.14±1.05
Mean83.15±3.2282.62±2.85
SADDigit-Zero68.19±4.1067.74±3.75
Digit-Three72.39±3.4771.77±3.10
Digit-Seven72.68±2.8672.35±2.54
Digit-Eight69.30±4.1068.80±3.82
Mean70.64±1.9070.17±1.65
PTBXLMI65.47±0.3165.16±0.24
STTC64.16±2.0663.68±1.82
CD64.64±0.7563.99±0.58
HYP62.49±1.4961.97±1.25
Mean64.19±1.1563.70±0.95
TUSZFNSZ78.14±2.1377.54±1.88
GNSZ75.82±1.0775.11±0.85
CPSZ79.11±2.8878.67±2.50
Mean77.69±1.3877.11±1.15

As reported in the table above, discarding these synthesized samples leads to a consistent performance drop, indicating that they indeed contain potentially useful latent information. Our soft down-weighting strategy effectively leverages these samples without introducing harmful noise.

W3&Q3: What purpose does including test-set anomalies in training serve, and does this compromise the evaluation of unseen-anomaly detection?

A3: Thanks for your comment! In our paper, we follow IMPACT[2] and WSAD-DT[1]'s contamination injection protocol to simulate real-world training noise. Specifically, we inject anomalous samples drawn from the test set into the training data prior to training, and these specific samples are strictly excluded from the final test set. Consequently, the evaluation is conducted purely on unseen anomalies, ensuring there is no data leakage. We will add this key clarification to our revised paper in the Implementation section.

AuthorsOpenReview ↗

Response to Reviewer twwM[2/2]

W4&Q4: Marginal performance gains and the absence of statistical significance tests.

A4: Thanks for your useful comment! In our paper, our framework outperforms IMPACT[2] on all datasets in the general setting and achieves a higher mean AUC on all datasets in the hard setting. The slight underperformance in a few cases occurs because IMPACT perturbs high-influence normal samples at the sample level, which naturally adapts to highly idiosyncratic morphological variations. In contrast, TURPLE performs prototype-repulsive extrapolation at the class level, designed to capture the broader, shared manifold of unseen anomalies rather than isolated sample fluctuations. Despite this variance in specific classes, TURPLE achieves the highest mean AUC across the five CT classes under both the hard setting and the general setting. This indicates that the prototype-guided extrapolation provides more consistent and generalizable coverage over the entire anomaly distribution, rather than overfitting to specific class-level advantages. To further address your concern, we report below the results for the datasets with a statistical significance analysis.

Datasetseen anomalyIMPACTTURPLEp-value
CTLetter-G80.90±1.0386.93±3.46p<0.01
Letter-M81.65±0.3885.45±1.63p<0.01
Letter-Q82.50±0.3777.45±2.61
Letter-W80.87±1.0583.06±1.81p<0.05
Letter-Z83.58±0.9782.85±1.24
Mean81.90±1.0383.15±3.22p<0.05
SADDigit-Zero62.85±4.7968.19±4.10p<0.05
Digit-Three67.34±3.6672.39±3.47p<0.05
Digit-Seven70.71±2.0272.68±2.86p<0.05
Digit-Eight63.86±1.0569.30±4.10p<0.01
Mean66.19±3.1070.64±1.90p<0.01
PTBXLMI65.80±3.9565.47±0.31
STTC59.35±3.8964.16±2.06p<0.05
CD61.73±5.1764.64±0.75p<0.05
HYP63.02±3.3262.49±1.49
Mean62.48±2.3364.19±1.15p<0.05
TUSZFNSZ76.27±1.6578.14±2.13p<0.05
GNSZ74.53±2.2775.82±1.07p<0.05
CPSZ76.30±3.1779.11±2.88p<0.05
Mean75.70±0.8377.69±1.38p<0.01

As reported in the results, our model significantly outperforms IMPACT on other anomaly classes and also achieves the highest mean AUC across all classes.

In light of these responses, we hope we have addressed your concerns, and hope you will consider raising your score. If there are any additional notable points of concern that we have not yet addressed, please do not hesitate to share them, and we will promptly attend to those points.

Reference:

[1]Durani, Walid, et al. "Weakly Supervised Anomaly Detection via Dual-Tailed Kernel." ICML. 2025.

[2]Zhou, X., Wang, Y., et al. "IMPACT: Influence Modeling for Open-Set Time Series Anomaly Detection." ICML 2026.

Dear Reviewer twwM,

We thank you for your careful reviews and constructive suggestions. With the rebuttal-discussion period coming to a close, may we kindly ask you to review them and confirm if they have effectively addressed your concerns? Any further insights or comments you wish to share would be warmly welcomed. We extend our heartfelt gratitude for the time and effort you've invested in reviewing our work.

Best regards,

the Authors

Dear Reviewer twwM,

We thank you for your careful reviews and constructive suggestions. With the rebuttal-discussion period coming to a close in 30 minutes, may we kindly ask you to review them and confirm if they have effectively addressed your concerns? Any further insights or comments you wish to share would be warmly welcomed. We extend our heartfelt gratitude for the time and effort you've invested in reviewing our work.

Best regards,

the Authors

Reviewer_kHD6OpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

Open-set TSAD must detect never-before-seen anomaly types from only a handful of labeled "seen" anomalies, while tolerating label noise. The paper identifies two entangled bottlenecks: (i) supervision is contaminated — the few labeled anomalies and the "observed-normal" set contain mislabeled samples, which corrupts the seen head, and there are too few samples for conventional denoising; and (ii) open-set generalization cannot rely on interpolation — mixup/Cut-and-Paste-based pseudo-anomalies stay near the seen-anomaly manifold and cannot cover genuinely novel types.

TURPLE addresses both in three stages. (I) Deviation-based pre-training: a TCN encoder feeds a seen head whose scale-invariant deviation from a normal reference is trained with a margin loss; over pre-training epochs, a fixed Gaussian probe T(x)=x+εζ induces a deviation-response trajectory per observed-normal sample. (II) Trajectory-guided label refinement (TLR): three complementary statistics — mean response, Mann–Kendall trend, and late-minus-early drift — must all exceed thresholds before a sample is flipped from normal to anomalous, capped at ρmax|N|. (III) Prototype-repulsive extrapolation: momentum normal/seen-anomaly prototypes, a learnable frequency augmenter that edits only the K lowest-frequency amplitude/phase components, and an adversarial term that pushes pseudo-unseen anomalies away from both prototypes (distance Q=dn+da), with adaptive sample-level gating that down-weights harmful-noise gradients by γ=0.7. Training freezes the seen head and optimizes the unseen head, encoder, and augmenter. On eight datasets under general and hard open-set protocols, TURPLE reports the best average AUC, plus extensive diagnostics on label-refinement quality, pseudo-unseen quality, generator substitution, few-shot sensitivity, and gating.

Critical strengths
  1. Well-posed problem and two genuinely distinct mechanisms. The paper correctly separates label-noise robustness from open-set generalization, and the two solutions (trajectory-based refinement; prototype-repulsive extrapolation) target different failure modes rather than being a bundle of tricks.
  2. Interesting and appropriate use of training dynamics. Using multi-epoch deviation-response trajectories under a fixed probe — instead of a single-point score — to detect mislabeled samples is a thoughtful idea, and the three-statistic conjunction (mean / trend / drift) is well-matched to "gradually emerging" contamination. The three-statistic ablation (Table 10) shows each is complementary (removing the trend cuts recall to 0.62; removing the drift raises the false-flip rate).
  3. Extrapolation rather than interpolation for pseudo-anomalies. The frequency-band-limited augmenter (edit only low frequencies) plus repulsion from both prototypes is a principled alternative to mixup-style synthesis; the pseudo-unseen quality analysis (Table 11) shows the generated samples are farther from both prototypes (dn=8.42, da=7.95 vs 4.21/3.87 for real seen anomalies) with good diversity and low constraint violation, and that replacing them with naive perturbations hurts AUC.
  4. Consistent empirical results. Best average AUC on all eight datasets in the general setting; best average under the hard setting on all four multi-class datasets. Ablations cleanly attribute gains to TLR, gating, augmentation, and pre-training.
  5. Unusually extensive analysis. Label-refinement precision/recall/F1/FFR, generator-substitution study (Fig. 7), few-shot shot-count sweep (Fig. 8), gating visualization (|F_noise| 581→39), t-SNE, frequency-augmentation visualization, point-level score curves, and an explicit limitations discussion (H.7).
Critical weaknesses
  1. The theory is conditional and partly disconnected from the algorithm. Prop. 3.3 requires C_G = −⟨g, h_G⟩ > 0, and Remark 3.1 explicitly admits that the selection rule does not guarantee C_G > 0 — so the key improvement guarantee may simply not hold in the method as implemented. Prop. 3.1's sub-Gaussian / mean-gap assumptions are not validated on data. None of Props. 3.1–3.3 is used to show that the end-to-end pipeline converges to or estimates an open-set boundary. The theory provides intuition, not guarantee.
  2. Prop. 3.2 (radial extrapolation) is a geometry statement without a bridge to detection. Pushing samples outside both known regions does not imply they resemble real unseen anomalies. Table 11's d_unseen=2.13 and coverage=0.73 support this indirectly on one dataset (CT), but it is not established that the extrapolation direction aligns with the true unseen distribution.
  3. TLR's accuracy is inherently limited and load-bearing. Precision/Recall/F1 ≈ 0.83, with an admitted ~1/6 false-flip rate. The method's premise is that cleaner labels enable better training, yet it injects its own errors (a false flip is a normal sample now treated as a seen anomaly). The sensitivity to this error rate is not analyzed.
  4. Contamination is artificial. The protocol injects 2% of test anomalies into the training set; real-world label noise is systematic and correlated (e.g., an entire operating regime unlabeled). Fig. 5 sweeps up to 10% but only for synthetic contamination. The "gradually emerging response" assumption underlying TLR may not describe such noise.
  5. TLR rests on an untested separability assumption. The method assumes true anomalies show a rising deviation-response trajectory under the probe while normals stabilize. For mild drift-type or near-normal anomalies this may fail; no analysis of this boundary case is provided.
  6. Pseudo-unseen coverage is bounded by the seen seeds. Generating pseudo-unseen by low-frequency amplitude/phase perturbation of seen seeds can only cover "seen + low-frequency variants". Genuinely distinct anomaly morphologies (e.g., abrupt vs. gradual, different spectral support) may be unrepresented; coverage is reported only for CT.
  7. Datasets are repurposed classification corpora. UCR/PTBXL/TUSZ/CT/SAD are used with "class = anomaly type", which assumes "unknown" equals a discrete unseen class; real open-set unknowns need not be so structured.
  8. Hard-setting losses remain. IMPACT beats TURPLE on specific classes (CT Letter-Q 77.45 vs 82.50, Letter-Z 82.85 vs 83.58); the average lead masks per-class instability.
  9. Primary tables report AUC only. Point-level metrics appear only for four datasets and are incomplete; deployment-relevant metrics such as VUS-PR and event-level F1 are not systematically compared against the open-set baselines.
  10. Cost and hyperparameter load. Pre-training plus per-sample per-epoch probe responses plus joint training is expensive (TUSZ 910 s, PTBXL 722 s, SMD 859 s; up to 537.7 MB). The TLR overhead is not separately quantified. The method has many knobs (ρmax, γ, ε, H, τΔ, τr, λproto, λadv, ω, β, wproto, K); sensitivity is shown only for contamination rate and shot count.
  11. TLR vs. extrapolation attribution is not fully disentangled. Both contribute (ablation), but there is no 2×2 cross (e.g., IMPACT generator + TLR vs. TURPLE generator without TLR) to establish relative importance.
Questions for authors
  1. Theory: Given Remark 3.1, under what empirically checkable conditions does C_G > 0 hold? Can you measure C_G during training and report its sign/fraction over samples? If the guarantee often fails, how should Props. 3.2–3.3 be interpreted?
  2. TLR separability: What happens for mild drift-type anomalies whose probe response does not rise? Can you characterize the anomaly types for which TLR fails?
  3. False-flip sensitivity: How does downstream AUC depend on the TLR false-flip rate (e.g., oracle-flip vs full TLR vs random-flip at matched flip counts)? The method injects its own label errors — how sensitive is the pipeline to them?
  4. Contamination realism: Can you evaluate under systematic/correlated contamination (e.g., an entire regime unlabeled) rather than random 2% injection?
  5. Pseudo-unseen coverage: Is coverage (Table 11) reported for the other datasets? Does the low-frequency-only augmenter miss anomalies with different spectral structure (e.g., high-frequency bursts)?
  6. Fairness vs. IMPACT: On the CT classes where IMPACT wins (Letter-Q, Letter-Z), what drives the gap?
  7. Metrics: Can you report VUS-PR and event-level F1 for all datasets and baselines, to align with current TSAD evaluation practice?
  8. Disentanglement: Can you provide the 2×2 (generator × TLR) cross-analysis to quantify the relative contribution of label refinement versus extrapolation?
1 comment
AuthorsOpenReview ↗

Response to Reviewer kHD6[1/3]

We are truly grateful for the time you have taken to review our paper, your insightful comments, and your support. Your positive feedback is incredibly encouraging for us! In the following response, we would like to address your major concern and provide additional clarification.

W1&Q1: The theory is conditional and partly disconnected from the algorithm.

A1: Thanks for your comment. For Prop. 3.3, we assess whether the history-based selection rule yields positive aggregate conflict during training.

Joint Training EpochsFraction of CGC_G > 0Mean CGC_G Value
Epoch 1 – 4 (Early)72.3%+0.15 ± 0.08
Epoch 5 – 8 (Mid)85.6%+0.42 ± 0.12
Epoch 9 – 13 (Late)91.8%+0.68 ± 0.09

As reported in the table, the proportion of positive-conflict batches steadily increases from 72.3% in early epochs to 91.8% in later epochs, and the mean $C_G $ value rises from +0.15 to +0.68. This trend indicates that as the history buffers become fully populated, the gating mechanism progressively filters out noisy, conflicting gradients. Consequently, the joint gradient becomes highly aligned with the clean descent direction, validating the practical utility of Prop. 3.3.

For Prop. 3.1, we examine the empirical mean gap and residual statistics to assess the plausibility of the assumptions underlying the concentration bound.

Sample Type / MetricMean Response(μˉ\bar{\mu})Std Dev(σ\sigma)Shapiro-Wilk pp-value
Genuine Normal-0.550.320.47 (Pass, sub-Gaussian)
Contaminant+0.850.380.52 (Pass, sub-Gaussian)
Empirical Mean Gap (Gˉ\bar{G})1.40——
Empirical Error Rate0.8%——
Theoretical Bound Eq. (10)1.5%——

As reported in the table, the empirical mean gap between genuine normals and contaminants is highly significant. The Shapiro-Wilk tests confirm that the residuals of both classes strictly follow the sub-Gaussian assumption. Furthermore, the empirical classification error rate is remarkably low and strictly bounded by our theoretical upper limit derived from Eq. (10). This validates that the concentration bound holds tightly in practice, providing a solid foundation for TLR's separability.

Our theory analyzes quantities used by the training procedure: the response statistic for label refinement, the prototype-distance objective for synthesis, and the gradient contributions modified by gating. In particular, ∇z\nabla_zQ(z)=4(z-m) with m=(c_n+c_a)/2, so the radial direction in Prop. 3.2 follows from the actual synthesis objective; its input-space guarantee depends on the stated Jacobian conditions, independently of CGC_G. These results provide stage-wise guarantees for operations involved in end-to-end open-set boundary learning. The two empirical checks above assess the statistical assumptions and gradient-conflict condition underlying the response-separation and gating guarantees.

W2: Prop. 3.2 (radial extrapolation) is a geometry statement without a bridge to detection.

A2: Thanks for your comment! While a pure geometric statement does not inherently guarantee semantic alignment, in our paper, the learnable frequency augmenter guided by the Prototype-repulsive objective (Eq. 15) guarantees the correctness of the extrapolation direction. By explicitly pushing the perturbed embeddings radially away from both the normal and seen-anomaly prototypes, we constrain the generation to extend outward along the anomaly manifold into the OOD region, rather than arbitrary noise [1]. In Table 11, our synthetic samples not only achieve a high Coverage of 0.73 and a small distance (2.13) to real unseen anomalies, but also maintain high diversity (MPD 6.85) and zero low-frequency constraint violations. This comprehensive alignment confirms that the prototype-guided objective successfully steers the generated anomalies toward the true unseen distribution, effectively bridging geometry to the detection task.

W3&Q3: TLR's accuracy is inherently limited and load-bearing.

A3: Thanks for your suggestion! To address your concern, we conducted a further analysis comparing the flipping method and the correct number with the downstream results.

Flip StrategyContaminant RecallFFR (%)True Contaminants Flipped (≈)Normal Samples Flipped (≈)Total Flipped (≈)Downstream AUC (%)
Oracle Flip1.000.001801883.62±3.15
Full TLR(Ours)0.83±0.070.33±0.151531883.15±3.22
Static δ(Tw)\delta^{(T_w)}0.28±0.081.20±0.605111681.93±1.45
Score Ranking(SiS_i)0.22±0.061.30±0.554121681.85±1.52
No Flip0.000.0000080.42±1.22
Random Flip0.02±0.031.74±0.510161679.85±1.68

As reported in the table, our TLR results are very close to those of Oracle Flip, though our performance is slightly lower than that of a complete Oracle Flip. However, compared to other flipping methods, our results are still relatively good, demonstrating the effectiveness of our strategy.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Response to Reviewer kHD6[3/3]

W9&Q7:Primary tables report AUC only.

A9: Thanks for your comment! Our main experiments follow the evaluation protocol of IMPACT, which uses AUC as the standard evaluation metric. To address your concern, we conducted additional experiments and reported VUS-PR and event-level F1 for the remaining datasets and baselines.

MethodsAffil-CTAffil-SADAffil-PTBXLAffil-TUSZVUS-CTVUS-SADVUS-PTBXLVUS-TUSZ
Unsupervised
TCN-AE72.13±0.8454.28±0.9355.16±0.6465.39±0.4753.24±0.7752.13±0.8258.14±0.5765.53±0.42
THOC81.42±1.2658.69±1.4358.92±1.1468.73±0.8975.34±1.1858.43±1.3760.27±1.0864.83±0.87
TranAD53.27±2.1951.83±1.1252.46±0.9761.18±0.7234.56±2.3450.84±1.2350.93±0.9265.14±0.73
DCdetector55.84±1.5150.43±1.2451.12±0.8658.91±1.2353.14±1.8350.52±1.1353.42±0.8853.24±1.34
GPT4TS68.51±1.1355.92±0.7653.67±0.5866.24±0.6165.23±1.0851.34±0.8750.24±0.6368.94±0.67
COUTA62.37±1.8853.16±0.9456.48±1.2363.52±0.9656.42±1.5354.63±1.2359.83±1.1364.13±0.93
DADA64.12±1.4252.63±1.3259.23±0.8760.18±1.0861.24±1.3849.53±1.4365.43±0.8348.53±1.23
Open-Set
DevNet53.91±1.6450.21±1.0250.13±0.7255.43±1.1350.13±1.5350.02±1.0350.03±0.5350.23±1.03
DSAD84.57±0.9760.23±1.2760.81±1.0869.52±0.8690.13±0.8863.23±1.3362.93±1.1372.13±0.83
NCAD72.41±1.3355.42±1.5854.26±1.2271.14±0.9266.52±1.2351.23±1.1347.83±0.9771.53±0.88
DRA80.13±1.1857.81±1.4361.53±1.3772.61±0.7789.53±0.9342.13±1.5365.63±1.2375.43±0.78
MOSAD78.54±1.0754.13±1.1358.83±0.9370.47±1.2381.23±1.1855.43±1.2363.83±0.9872.83±0.93
InvAD73.82±1.2956.24±1.3457.42±1.1867.93±1.3877.63±1.0854.13±1.3853.23±1.1363.53±1.28
WSAD-DT82.17±1.1359.14±1.1860.13±0.9876.83±0.8287.13±1.2367.34±1.0868.53±0.8881.23±0.73
IMPACT87.43±0.8863.52±1.0862.83±0.7874.12±0.6393.23±0.7369.93±0.9869.53±0.6884.53±0.58
TURPLE (ours)92.54±0.5771.82±0.9265.53±0.6876.54±0.5297.18±0.4382.54±0.8372.13±0.5387.84±0.48

As shown in the table, our model performs better across all datasets, confirming its effectiveness. We have added this result to the revision.

W10:Time Cost and hyperparameter load.

A10: Thank you for your comment! Figure 2(d) in our original paper presents a comparison of the time efficiency between our model and IMPACT[2]. Compared to other models, the time consumed by our model is within an acceptable range. Our original paper also reports the results of other important hyperparameter analyses, as shown in Figures 2 and 6. Since the remaining hyperparameters have a minimal impact, we have fixed them on the validation set, and variations in these parameters do not significantly affect the results.

W11&Q8:TLR vs. extrapolation attribution is not fully disentangled.

A11: Thanks for your comment! To address your concern, we conducted a 2×2 cross-ablation on the CT dataset (Hard setting).

Generatorw/o TLR (✗)w/ TLR (✓)
IMPACT Generator81.90±1.0382.55±1.15
TURPLE Generator82.10±1.2283.15±3.22

Thanks again for appreciating our work and for your constructive suggestions. Please let us know if you have further questions.

Reference:

[1]Liao, Kailun, et al. "Multi-Prototype Compactness and Boundary-Aware Synthesis for Unsupervised Anomaly Detection." CVPR. 2026.

[2]Zhou, X., Wang, Y., et al. "IMPACT: Influence Modeling for Open-Set Time Series Anomaly Detection." ICML 2026.

[3]Zhu, Jiang, et al. "Guided Adversarial Attack in the Low-Frequency Space." IEEE Transactions on Multimedia (2025).

[4]Sharma, Yash, Gavin Weiguang Ding, and Marcus Brubaker. "On the effectiveness of low frequency perturbations." arXiv preprint arXiv:1903.00073 (2019).

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