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Under review as a conference paper at ICLR 2027

Detecting Time-Series Anomalies with Score Models Alone

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Abstract

Diffusion and score-based generative models expose the gradient of the log-density, , not the density itself. Can such score-only models detect anomalies in time series, and what exactly can they detect? First, the capability: a directly parameterized score network, scored by the window-averaged Hyvärinen statistic , reaches VUS-PR on the TSB-AD univariate benchmark, with no statistically significant difference from the strongest baseline PaAno (which stays ahead under a buffer-free control), at under a third of its measured runtime; on the multivariate suite it is mid-field. The divergence term is load-bearing and significant: over the same network's score norm (). Second, the limits: we prove the population detection gap equals one half the Fisher divergence plus a signed Fisher-information correction, naming a blind spot of the upper-tail test that more data cannot remove: anomalies sharper than normal data invert the statistic whenever , and we observe an inversion consistent with this class on a real sensor flat-line. Third, the mechanism: window aggregation estimates the statistic's population expectation (i.i.d. window model), and footprint-scale aggregation () performs near the best tested scale in our synthetic length-group averages. Fourth, an equal-treatment audit: the same aggregation lifts five saved-score baselines by – VUS-PR and reorders the leaderboard (the lift surviving a buffer-free control), so part of the apparent ranking is output post-processing. In our matched energy-network comparison on the univariate suite, the two statistics show no statistically significant difference; the score-only statistic is useful when no energy readout is available.

Primary area:
learning on time series and dynamical systems
Keywords:
Time-series anomaly detection, Score-based models, Denoising score matching, Hyvärinen score, Fisher divergence, Window aggregation, Energy-based models

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_M3mvOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper introduces an unsupervised time-series anomaly detector built entirely on a score function learned with denoising score matching. Each subsequence is scored with a window-averaged Hyvärinen statistic J, which needs neither a partition function nor an energy. The paper also gives a theoretical analysis of when this statistic detects anomalies and a rule for choosing the smoothing length. The authors claim that this score-only approach performs on par with the strongest baseline, PaAno, on the univariate benchmark (0.588 vs 0.584 VUS-PR; no significant difference), at under a third of its runtime, while it ranks in the middle on the multivariate benchmark.

Critical strengths
  1. The paper gives an exact formula for how much higher the statistic is on anomalies than on normal data. It shows that detection works when anomalies differ strongly from normal data, and fails when anomalies are more concentrated than normal data. It also shows a real example consistent with this, a low-variance flat-line anomaly on which the statistic drops instead of rising.

  2. The error bound in Proposition 1 does not assume that the learned score is the gradient of an energy. Hence, the method works with any trained score network, including diffusion-style models where no likelihood is available. This makes it an easy way to reuse an existing score model as an anomaly detector, at the cost of one score evaluation and a divergence estimate per window.

  3. The method works well even though the network is a simple MLP trained with standard denoising score matching. On the univariate benchmark, even the energy-parameterized variant (0.561 VUS-PR) comes close to PaAno (0.584), which is considerably more elaborate. It is also about 0.07 or more ahead of all the other neural baselines the authors ran, and it stays ahead when the paper's audit applies the method's moving-average smoothing to the scores of five of them.

Critical weaknesses
  1. The paper says all hyperparameters are chosen on the tuning split and the architecture is fixed to the energy-parameterized MLP, but the main claims (abstract, contributions, and the comparison with PaAno) use the direct score network instead. In the tuning split, the energy network outperforms the direct network (0.514 vs 0.504 VUS-P; Tables 4 and 18). The direct network is better only on the evaluation set (0.588 vs 0.561), which should be used to report results, not to choose between models. This choice matters because, against PaAno, the direct network is ahead by 0.004, while the model selected on the tuning split is behind by 0.023.

  2. The method performs among the best on the univariate benchmark, but the paper does not show that the Hyvärinen statistic J itself is the reason. Most of J's own gain comes from the moving-average smoothing, which takes the direct network from 0.506 without smoothing to 0.588 with it, and the paper's audit shows the same smoothing also helps the baselines. In addition, when the network provides energy, that energy performs at least as well as J (0.577 vs 0.561 for the energy network). The contribution therefore rests on the case where no energy is available.

  3. PaAno is reported as averaged over three seeds, but it was effectively run with only one. Its configuration fixes the seed to 2021 (HP_list.py, line 143), PaAno applies it when training starts (PaAno_PAI.py, line 616), and the experiment runner never passes the run seed, so the three runs are identical. This can be seen in the paper itself, where PaAno is reported as 0.584 ± 0.000 (Table 1) and some of its multivariate scores have a standard deviation of exactly zero (Table 8). When I ran PaAno on one series with four different seeds, its VUS-PR ranged from 0.574 to 0.620. The statistical tests are still valid, but the claimed lead over PaAno (0.588 vs 0.584) may depend on this single run.

Questions for authors

Q1: Was the direct score network chosen as the main model before you saw the evaluation results, and if so, on what basis?

Q1.1: Following the tuning split as described would select the energy network, yielding a main result of 0.561, which is below PaAno (0.584) and the same network's energy readout. How would this change the claims of the paper?

Q2: Is there a setting where J clearly beats an energy readout, or where the statistic itself, and not the smoothing, explains the gain over the baselines?

Q2.1: For example, how do pointwise J and pointwise energy compare with each other and with the smoothed baselines?

Q3: In Section 6, the paper reports the method as "TOST-equivalent" to PaAno within ±0.05. This test treats the 350 series as independent, but they come from only 23 datasets, and your own source-clustered interval ([−0.109, +0.092]) is wider than the margin. Will you remove the equivalence claim or redo the test to account for the source datasets?

Q4: Can you confirm that PaAno's fixed seed overrides the experiment seed in all three runs?

Suggestion: Please rerun PaAno with different seeds, report its mean and standard deviation, and check whether the direct network is still ahead.

Q5 premise: The paper states that the runtimes are directly comparable because each job used a single GPU worker. However, the launch scripts run 16 to 20 jobs in parallel on 8 GPUs, so several models seem to have shared the same GPU at the same time, and not always in the same way (16 parallel jobs for the direct network, 20 for PaAno). Timing both methods one at a time on a single GPU for 40 time series from the benchmark, I found a 2.0x speed-up over PaAno, instead of the reported 3.4x, although my hardware is different, which may also explain part of the gap.

Q5.1: Were the timing runs done with one job per GPU?

Q5.2: If not, can you measure the runtimes again under controlled conditions?

2 comments
AuthorsOpenReview ↗

Reply to Reviewer M3mv

Thank you. Your review identified real protocol problems, including a seed bug in the benchmark's own PaAno configuration. We fixed all of them, and the main result holds under the stricter protocol you asked for.

W1 / Q1. Model choice. The direct network was chosen after evaluation results were available, because a model with no energy is the case the paper is about. The revision says so and reports results in protocol order (Table 1):

  • Tuning split. It favours the energy network, though not significantly (0.517 vs 0.505, p = 0.31).
  • Tuning-selected readouts. 0.577 (energy; −0.006 vs PaAno, p = 0.90) and 0.561 (J; −0.023, p = 0.11).
  • Post hoc. The direct network reaches 0.588 (+0.005, p = 0.57).

Q1.1. How the claims change. The claim survives the strict protocol: whichever row one takes, no difference from PaAno is detected under VUS-PR, and that includes the tuning-selected model. We now also report all four metrics (Table 34). PaAno is significantly ahead under VUS-ROC and AUC-ROC, and the abstract says so.

W2 / Q2. J vs smoothing. You were right that averaging carries most of the gain, and the paper now says so. We tested every comparison you asked about:

  • Pointwise. Pointwise J (0.506) is not distinguishable from the pointwise energy (p = 0.56).
  • Energy vs J. The energy edges J per series but not under source clustering: U +0.017 (clustered p = 0.67); M +0.021 (0.18) and +0.018 (0.29).

This is why the paper's claim is about score-only models, not about J beating an energy. When a model has an energy, use it. When it has only a score, as diffusion models do, this paper shows it is enough to reach PaAno-level VUS-PR.

Q2.1. Smoothed baselines. Equal averaging lifts all five audited baselines by 0.017–0.233. Every gain is significant per series and under source clustering, and the ranks change (Table 4). That is a benchmark finding of its own.

W3 / Q4. PaAno seeds. Confirmed. TSB-AD's HP_list.py fixes seed = 2021 and calib_seed = bank_seed = 42, overriding the run seed. We re-ran with all three tied to the run seed:

  • 0.583 ± 0.002 (U) and 0.404 ± 0.002 (M);
  • the paired difference is essentially unchanged (+0.005 vs +0.004).

Q3. TOST. Withdrawn. It passes per series (p = 0.007) but not clustered by source (p = 0.19).

Q5. Timing. The earlier numbers came from shared-GPU sweeps, so "directly comparable" is removed. We re-measured one job at a time on one NVIDIA T4 over 40 random series: PaAno takes 3.3× as long on average, 1.9×–5.0× per series (Appendix I). Your 2.0× is inside that range.

We also checked tuning/evaluation overlap. Thirteen tuning series repeat an evaluation channel, and σ selection is unchanged without them.

Every protocol issue you raised is now fixed and documented, and the central result holds under the stricter analysis. We would be grateful if you would reconsider your score on the revised paper.

Thank you for the detailed response. I checked the revised PDF. The PaAno re-seeding (Table 31), the controlled timing (Appendix I), the withdrawn TOST, the protocol-ordered Table 1, and the ROC disclosure in the abstract address the protocol issues I raised, and I appreciate the transparency. However, these corrections remove the paper’s main empirical claim without replacing it, so my overall assessment is unchanged.

The headline result is now a null result. The original submission claimed parity with PaAno and a small lead. The revision correctly claims “neither a lead nor a tie,” and PaAno is significantly ahead under VUS-ROC and AUC-ROC. The rebuttal’s statement that a score-only model is “enough to reach PaAno-level VUS-PR” contradicts this. With a source-clustered CI of [−0.110, +0.092], the benchmark cannot distinguish methods $\sim$0.1 apart, so “no detected difference” is weak evidence of anything. In addition, the network, the readout, and the decision to sweep σ\sigma were all influenced by evaluation results. The protocol-selected model is the energy network, for which PaAno is nominally ahead, with a runtime advantage of about 2×2\times, not 3.3×3.3\times (right?).

The proposed statistic is not what drives performance. The divergence term, which is the object of Corollary 1 and what distinguishes J from the score norm, adds +0.023 on TSB-AD-U. This is not significant under clustering, and 84% of it comes from one source (Exathlon). Without it, the method is the MSMA score norm at a single scale plus a moving average, as the revision itself acknowledges. Before averaging, J is not distinguishable from the smoothed CNN, DTE, and LSTM-AD. After equal averaging, its lead survives clustering only over TranAD. When an energy is available, the energy readout is at least as good. The theoretical contribution is a one-step corollary of a classical identity, and its predicted failure mode is illustrated on a single series.

What remains is the averaging audit, which is a useful benchmarking observation, together with a mid-field multivariate result and a conformal alarm the authors describe as “not usable as is.” I do not think this is enough for acceptance, and I keep my rating.

Reviewer_KJtWOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2(+1)
Soundness
2
Read review
Paper summary

The paper investigates whether time-series anomalies can be detected using a learned approximation to the normal-data score field s_p(x) = grad log p(x), without evaluating a normalized density or learning an explicit scalar energy. It applies the classical Hyvarinen statistic J(x) = div s(x) + 0.5 ||s(x)||^2 to sliding-window embeddings and temporally aggregates the resulting scores. A signed mean-gap decomposition explains why positive Fisher divergence alone does not ensure that anomalies receive larger scores: some alternatives, including variance collapse near the normal mean, can decrease the statistic. The analysis also accounts for learned-score error and the noise-smoothed training target rather than treating the ideal population identity as an automatic guarantee for the learned detector. Experiments on the univariate and multivariate TSB-AD suites assess score readouts, aggregation, runtime, and calibration. The direct score-only detector is competitive on the univariate suite, while multivariate gains are more limited. Applying the same aggregation to saved baseline scores shows that post-processing materially affects comparisons. The paper also reports failure cases and substantial false-alarm inflation outside the assumptions of its conditional calibration result. Centered aggregation makes the evaluated procedure an offline detector rather than a validated causal alarm system.

Critical strengths
  1. A useful bridge from score matching to one-class detection, with an explicit failure interpretation. The decomposition Delta = 0.5 F(q||p) + 0.5[I(p) - I(q)] distinguishes a nonnegative distributional discrepancy from the direction of the expected-score shift relevant to upper-tail detection. The discussion of variance-collapse failures, learned-field error, and the smoothed target helps prevent an overly broad interpretation of score-only detection. The contribution is consequential as a coherent detection interpretation and empirical study, rather than as a new score-matching identity. The main evidence appears on pp. 4-6 and in Appendix A.

  2. Competitive univariate results accompanied by a consequential comparison audit. Tables 5-6 report VUS-PR of 0.5879 for the direct detector and 0.5837 for PaAno, with no established superiority in the paired comparison (reported p = 0.643). The direct score norm achieves 0.5654, supporting a univariate benefit from the divergence term. The equal-aggregation audit is particularly valuable: Table 27 retains substantial gains for baselines on a common 246-series cohort, showing that the result is not merely a coverage artifact. The paper also reports lower mean fit-plus-scoring time than PaAno in its measured setup, 3.0 versus 10.1 seconds. Together, these results establish a credible practical baseline and improve how benchmark rankings should be interpreted. They do not establish universal superiority; buffer-free AUC-PR favors PaAno, 0.5516 versus 0.5212.

Critical weaknesses
  1. The connection between conditional theory and operational guarantees remains limited. The independent-sample concentration result does not directly cover dependent, overlapping scores; Appendix A.5 reports a diagnostic with lag-one correlation of 0.945 and variance inflation of 21-107. The geometric footprint follows from overlap, but dependence can change aggregation variance and hence the SNR curve or near-optimal aggregation width. Invariance of these latter conclusions needs additional assumptions or narrower wording. Calibration is also not operationally resolved: Table 29 reports mean FAR of 0.224 at nominal 0.01, falling only to 0.053 with rolling recalibration while TPR decreases from 0.733 to 0.391. These limitations are acknowledged and do not invalidate the conditional theorems, but they restrict what the analysis guarantees about deployed detection. Appendix B.1 additionally appears to fit z-score statistics on the whole training prefix before reserving calibration windows. The exact preprocessing/splitting order requires clarification because calibration and future test observations may not be treated symmetrically; this is not a confirmed implementation defect.

  2. The incremental contribution is uneven across settings. The statistic, score-matching identity, concentration tools, and conformal rank argument are established, so acceptance rests primarily on the detection interpretation and empirical evidence. That evidence is strongest for univariate data: on the multivariate suite, Table 8 reports 0.4272 for the direct full statistic versus 0.4354 for the same network's score norm. Aggregation improves the direct detector by only 0.0059 there, compared with 0.0814 on the univariate suite. The paper appropriately describes multivariate performance as mid-field, but the reversal limits the generality of the proposed readout's benefit. Results from a separate energy-parameterized network should not be used to strengthen the direct score-only claim. A clearer account of when the divergence term helps would materially strengthen the contribution.

Questions for authors
  1. Are z-score statistics fitted before or after the last 20% of prefix windows are reserved for calibration? How are overlapping windows across the fit/calibration boundary and full-series period estimation handled? A limited comparison using fit-only normalization and an appropriate boundary gap would help distinguish temporal drift from other departures from exchangeability. This question does not presume that Theorem 3 is incorrect.

  2. Can you report paired uncertainty for the multivariate difference between the full statistic and the score norm, and explain whether the reversal is associated with dimension, divergence-estimation error, or particular data types? Existing ablations or a focused analysis would be sufficient; a new large-scale benchmark is not requested.

  3. Can you distinguish more explicitly between the known-length synthetic diagnostic and the deployed label-free aggregation width? The geometric footprint itself is unchanged by dependence, but can you qualify the claim that the rise-then-dilute behavior and near-optimal aggregation scale remain unaffected when covariance changes the aggregation variance? This clarification affects the theoretical interpretation; developing a new causal window-selection algorithm would be future work, not a required revision.

2 comments
AuthorsOpenReview ↗

Reply to Reviewer KJtW

Thank you for the most technically probing review. Each of your questions now has a direct experiment behind it (Appendix J), and the answers strengthen the paper.

W1a. Dependence.

  • Theorem 2. Its takeaway now states that it assumes independent windows and does not by itself explain the measured gain.
  • Dependence quantified. Lag-1 autocorrelation is 0.945, and variance inflation is 21–107 (Appendix A.5).
  • Footprint. "Unaffected" is withdrawn; the footprint is now a reference scale.
  • Synthetic check. A dependence-aware signal-to-noise ratio reproduces the optimal length exactly at L = 30 and moves the right way at L = 100 (Table 33). We report it as a partial explanation.

W1b. Calibration. We diagnosed it rather than leaving it unexplained. The false-alarm rate at α = 0.01 is 0.224, and we removed the candidate causes one at a time:

  • Overlap. Calibration values overlapping the test region are not the cause: 0.151 → 0.161 without them, on the 777 series–seed pairs where this can be tested.
  • Other causes ruled out. Neither normal points near anomalies (0.151) nor prefix anomalies (0.162) is the cause.
  • What remains. The rate rises with distance from the prefix (0.137 → 0.179), which is consistent with drift. It is already 14× nominal at the prefix, which points to serial dependence in the calibration set.
  • Short prefixes. The remaining 273 pairs (median 100 calibration values) run at 0.431.

This tells practitioners why split-conformal fails on TSB-AD, a result of independent value. We present the detector honestly as an offline ranker.

Q1. Normalization order. The z-score was fitted on the whole prefix. The control fits it on the training windows only, with identical training and calibration windows, over 3 seeds:

  • VUS-PR +0.003 (CI [−0.002, +0.011]; clustered [−0.004, +0.011]);
  • false-alarm rate 0.216 vs 0.224.

Normalization order has no measurable effect on accuracy or calibration. The period estimate follows TSB-AD's label-free convention for every method.

W2a / Q2. TSB-AD-M reversal. Full J and the score norm are not distinguishable on M (−0.008, CI [−0.026, +0.010]). We checked each possible cause:

  • Probe noise. Ruled out: 16 probes changes the result by +0.002.
  • Data domain. The difference is not significant in any domain.
  • Dimension. It is confounded with source, so we claim no dimension effect.

W2. Averaging on M. The +0.006 is not a null but opposite effects:

  • averaging helps on Sensor (+0.031, p = 0.005) and Medical (+0.041, p = 0.003);
  • it hurts on Facility (−0.066).

On U, the gain survives leaving out any single source (+0.054 to +0.087).

W2b, established tools, offline.

  • Energy-network results now appear only as the tuning-selected model.
  • We agree the tools are standard. The contribution is what they show together: an exact account of a score detector's blind spot, a measured decomposition of where accuracy comes from, and a benchmark audit.
  • The average is centered, so the detector is offline. We state this up front.

Q3. The known-length synthetic diagnostic is now separated from the deployed label-free width (Section 6.3).

Thank you for the detailed responses. My concerns are addressed. The revised paper is easy to follow, so I raised presentation score.

Reviewer_3tXNOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2(+1)
Soundness
2
Read review
Paper summary

This paper proposes a score-based approach to time-series anomaly detection. Rather than explicitly modeling an energy function, the method directly learns the score field of the data distribution and uses the resulting Hyvärinen score as an anomaly detection statistic. Through theoretical analysis, the authors characterize the expected separation between normal and anomalous distributions and identify conditions under which the statistic fails to distinguish them. The proposed approach is evaluated on the TSB-AD benchmark, achieving strong performance on univariate time series but moderate performance on multivariate time series. Furthermore, the experiments show that detection performance tends to improve when the aggregation window length approximately matches the anomaly's score footprint.

Critical strengths

1. Competitive performance on univariate anomaly detection. The proposed score-only model achieves competitive performance on TSB-AD-U.

2. Clear theoretical and empirical characterization of the method's capabilities and limitations. The paper provides detailed theoretical analyses of when the Hyvärinen score can distinguish anomalies and when it fails. These limitations are further supported by empirical observations, including failure cases involving low-variance anomalies.

3. Extensive empirical evaluation. The paper conducts extensive experiments, including comparisons with numerous baselines, component ablations, synthetic benchmarks, etc.

Critical weaknesses

1. Insufficient justification for the computational overhead and methodological contribution of the divergence term. While DSM avoids the costly divergence computation during training, the proposed statistic reintroduces it at inference. It remains unclear whether the performance gain justifies this overhead, raising questions about the practical benefits and methodological novelty of using the full Hyvärinen score.

2. Limited multivariate performance and overstated claims. The direct net model shows relatively weak performance on TSB-AD-M (Table 1). However, Section 6 describes the proposed statistics as among the strongest methods on both benchmarks, which may overstate the results. The performance claims should be more carefully qualified.

3. Misleading attribution of energy-based results to the proposed score-only approach. Although the paper's central contribution is score-only anomaly detection, Section 6 presents the stronger results from the energy-based model as part of the proposed approach's overall performance, particularly on multivariate data. This potentially overstates the effectiveness of the score-only method and obscures the actual contribution of the paper.

4. Lack of clarity and organization. The overall presentation is difficult to follow. For example, Section 2 lists numerous related studies without clearly establishing their connections to the proposed approach. The coverage, seed, and researcher-degree-of-freedom disclosures in Section 6 interrupt the discussion of the main results and may be better placed in the experimental setup or appendix.

Questions for authors
  • How does the similar signed decomposition of the likelihood support the claim that JpJ_p is not a repackaged likelihood? (Section 4.1)
  • Why are the window aggregation results for the proposed direct score network omitted from Table 2?
2 comments
AuthorsOpenReview ↗

Reply to Reviewer 3tXN

Thank you. Your review pushed us to remove every overclaim, and we did. We hope the revised paper earns a fresh assessment, because its contribution is now clearer than before.

W1. The divergence term. You were right that it is not where the accuracy comes from.

  • Cost. It is 7.6% of fit-plus-score time; scoring alone is about 9× slower.
  • Gain on TSB-AD-U. +0.023 over the score norm (p = 0.025 per series), not significant under source clustering (p = 0.29), and 84% from Exathlon.
  • Gain on TSB-AD-M. None (−0.008, clustered CI [−0.040, +0.022]).

Section 6.2 says this plainly. The paper's value does not rest on the divergence. It rests on three results:

  • A signed detection gap. It holds for J and explains when score-based detectors miss anomalies; a real flat-line series shows the predicted drop of 1.4 normal-window standard deviations.
  • A score-only detector with no detected difference from PaAno under VUS-PR at a third of the runtime.
  • The averaging audit. Equal smoothing lifts five baselines by 0.017–0.233, every gain significant under source clustering, and reorders them.

The identity is classical, as we now say. Its use to characterize what a score detector can and cannot detect is new.

W2. Multivariate. Agreed, and corrected. TSB-AD-M is described as mid-field throughout (direct network 0.427; AxonAD 0.494, against our 0.472 on its 162 series).

W3. Energy-network credit. Agreed. Tables 1–2 report the energy network separately as the tuning-selected model, and no score-only claim uses its numbers.

W4. Presentation. The paper is reorganized:

  • related work rewritten as contrasts (Section 2);
  • a pipeline figure before the method (Figure 1);
  • all disclosures collected in Section 5;
  • results organized by question (Sections 6.1–6.5).

Q1. J vs likelihood. The likelihood gap has the same form, with entropy in place of Fisher information. J is its score-only counterpart: it needs no normalizing constant or ODE solve, which is exactly what a diffusion model lacks. We do not claim J sees what a likelihood cannot. We claim it gives the same kind of exact account where no likelihood is available (Section 4.1).

Q2. Direct-network rows. Added to Table 3. Averaging raises direct-net J from 0.506 to 0.588 (+0.081, clustered CI [+0.032, +0.126]); the score norm goes from 0.494 to 0.565.

Every point you raised is now answered in the paper, and the claims that remain are supported under source-clustered tests. We would be grateful if you would reconsider your score in light of the revised paper.

Thank you for your detailed responses to each of my concerns. I have carefully reviewed your rebuttal and the revised manuscript. I appreciate that the manuscript is now much clearer and easier to follow, and I will increase my presentation score accordingly. I also appreciate the more transparent reporting of the proposed method's performance and limitations.

However, I remain unconvinced that the central contribution is sufficiently supported by the experimental results. In particular, the additional computational cost of the divergence term does not appear to be adequately justified by its performance gains, and the comparisons with energy-based models do not establish a clear advantage or necessity for the proposed Hyvarinen-score-based approach. Therefore, I will maintain my overall rating.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Rebuttal Revision after taking feedback from the reviewers

We thank the reviewers. Their reviews were sharp and, in several places, right. We fixed every problem they found. We think the corrected paper is the stronger paper, and here is why it should be accepted.

1. A score model is a competitive time-series detector, at a third of the cost. Diffusion and score models are now the default generative backbone, but they give no likelihood to threshold. We show that a score network with no energy reaches 0.588 VUS-PR on TSB-AD-U, with no detected difference from the strongest re-run baseline (PaAno, 0.583). It does this at under a third of PaAno's runtime (3.3× faster in a controlled one-job-at-a-time run). The network the tuning split selects also shows no detected difference (0.577, p = 0.90).

2. An exact, testable account of what a score-based detector cannot see. The expected gap of the Hyvärinen score is half a Fisher divergence plus a signed Fisher-information term (Corollary 1). It tells practitioners precisely when an upper-tail detector fails: anomalies sharper than normal data can score lower. We see this on a real flat-line series, a drop of 1.4 normal-window standard deviations in every seed. To our knowledge, existing score-based detectors (MSMA, DTE, JuRe) come with no such statement.

3. A benchmark finding that matters beyond our method. Applying the same output averaging to five re-run baselines raises every one of them, by 0.017–0.233 VUS-PR. Every gain is significant under source clustering, and the averaging reorders the baselines. Part of what TSB-AD rankings measure is therefore post-processing, and fair comparisons should equalize it. We also found that TSB-AD's default PaAno configuration silently fixes its seeds, which affects anyone reporting PaAno with seeds.

4. A standard of evidence the field can reuse. Every comparison is reported per series and clustered by source, under all four threshold-free metrics, with leave-one-source-out and results in protocol order. All code and per-series outputs are released.

What we corrected:

  • PaAno re-seeded: 0.583 ± 0.002 (U), 0.404 ± 0.002 (M).
  • Equivalence and lead claims withdrawn; PaAno leads under ROC metrics (Table 34).
  • The post-hoc model choice is disclosed, with the tuning-selected network reported first (Table 1).
  • The divergence term is reported as adding little.
  • TSB-AD-M is called mid-field.
  • "Unaffected by dependence" is withdrawn.
  • Conformal over-alarming is diagnosed (Appendix J).

None of the corrections changes points 1–4. They make those points trustworthy. We hope the reviewers will judge the revised paper on what it now claims and supports, and reconsider their scores accordingly.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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