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Under review as a conference paper at ICLR 2027

SPARCE: Sparse Counterfactual Attribution via Gradient-Guided Diffusion for Time-Series Root Cause Analysis

Abstract

We introduce a novel approach to root cause analysis (RCA) in multivariate time-series anomaly detection, the task of identifying which features are responsible for a fault, not merely that one occurred. Our key observation is that identifying the sensors responsible for an anomaly can be framed as finding the minimal sparse edit to an anomalous window that restores it to the normal data manifold. Existing attribution methods rely on marginal feature perturbations or finite nearest-neighbor retrieval. Both produce out-of-distribution counterfactuals that violate the conditional dependencies inherent in real monitoring systems. We propose SPARCE (SParse Attribution via Reverse diffusion Counterfactual Explanation), which approximates this minimal-edit problem by injecting gradient-based guidance into the reverse process of a conditional score-based diffusion model trained exclusively on normal system behaviour. At each denoising step, the guidance jointly optimizes a denoising-consistency regularizer that steers the restoration toward normal behaviour and L1 sparsity penalty that encourages concentrated sensor edits. The root-cause attribution map emerges as the pointwise difference between the anomalous input and the diffusion-restored output, providing a jointly coherent explanation without per-sensor inference passes. SPARCE attributes observable deviations, which under propagation include downstream sensors, and is model-agnostic with respect to the anomaly detection backbone. We give sufficient conditions under which the attribution readout separates the deviating sensors. Experiments on SWaT, WADI, MSDS, and SMD demonstrate that SPARCE achieves state-of-the-art performance across Top-K Recall, CW-RCS, and TemporalHM metrics, improving Top-3 Recall by 13.2% over the strongest baseline on SWaT.

Primary area:
learning on time series and dynamical systems
Keywords:
root cause analysis, multivariate time series, anomaly detection, diffusion models, counterfactual explanation, feature attribution, explainable ai

Reviews

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1234this paper, Top 17%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
Reviewer_BJAoOpenReview ↗
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2
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Paper summary

SPARCE addresses root cause analysis for multivariate time-series anomalies as a sparse restoration problem. A diffusion model is trained only on normal windows. At inference, sampling starts from Gaussian noise and is steered by a gradient that combines two terms: a self-supervised denoising score SθS_\theta and an L1 distance to the anomalous window. The 30 restorations are averaged, and each sensor is ranked by its average absolute difference from the anomalous window. The paper reports state-of-the-art Recall, CW-RCS and TemporalHM on SWaT, WADI, MSDS and SMD. It also gives a conditional recovery theorem and a synthetic Structural-VAR benchmark with known roots.

Critical strengths
  • "Smallest edit that makes the window normal" is easy to interpret. It is a principled alternative to perturbing one sensor at a time, which breaks cross-sensor dependencies.
  • The paper clearly separates observable deviations from initiating faults (Prop. A.4, Sec. 5.4), which many RCA papers don't.
  • Four datasets, five detector backbones, matched aggregation for all baselines (Table 4), contamination tests, and restoration diagnostics such as validity and edit concentration.
  • the paper also discusses useful negative findings. Without gradient normalization, Top-3 Recall drops to 0.044; guiding at all steps hurts. Both are useful to practitioners.
Critical weaknesses

[W1] The baseline comparisons are unclear. A simple z score deviation ranking (Appendix Table 19) reaches 0.521 R@3 on SWaT beating every Table 1 baseline except CondAttr. It also outperforms the reported WaveStitch-RCA results on all four datasets and CSDI-RCA on three. Also, Table 1 mixes published numbers with reproduced numbers causing some confusion on baseline implementations.

[W2] The benefit of input specific sparse restoration is not fully isolated. Removing the L1 term removes the anomalous input from generation entirely, since sampling starts from noise with c = 0. Yet Recall@3 stays at 0.588, against 0.608 for the full method. This suggests much of the performance may come from subtracting a learned normal reference rather than building a repair specific to the input. This ablation also removes input anchoring and sparsity at the same time, so it cannot separate their contributions.

[W3] The role of the anomaly detection backbone could be explained more clearly. In SPARCE, the VAE detector does not seem to enter attribution (Sec. 3.1, Sec. 4.2). It only selects which windows are evaluated and defines restoration validity. For other baselines it seems that the detector is the model being explained, so it may limit their attribution quality.

[W4] The theory in the paper seems disconnected from the implemented method. The recovery theorem A.6 applies to approximate minimizers of the objective. SPARCE instead averages the outputs of a heuristic guided sampler, and the required optimization gap condition H3 is not established for it. Normalized guidance depends only on the ratio λs/λm, while the theoretical target depends on their absolute values.

Questions for authors

Q1. Can deviation ranking and per sensor reconstruction using SPARCE's own diffusion model be included in the main comparison (Table 1)?

Q2. Could the authors state which baseline numbers were taken from prior work and which were reproduced, and how a common evaluation protocol was ensured?

Q3. How does a cached input-independent restoration, reused across windows, compare with the full method?

Q4. Can a tractable example (e.g., a Gaussian prior) compare the actual guided sampler, including averaging over n draws, with the objective's minimizer or target distribution?

Q5. What changes if training explicitly includes all-hidden masks (for example, conditioning dropout as in classifier-free guidance) and inference is left unchanged?

Q6. Since SPARCE does not require the detector for attribution, could results be reported on all ground-truth anomalous windows without detector-based filtering? Could the baselines also be evaluated with a detector of comparable capacity to SPARCE's diffusion model?

6 comments
AuthorsOpenReview ↗

Evidence and clarifications (1/2): deviation and per-sensor baselines, baseline provenance, learned reference vs. sparsity

We thank the reviewer for the detailed review and for recognizing the formulation, the separation of observable deviations from initiating faults, and the breadth of the evaluation. We provide new experiments and clarifications below.

W1 / Q1. Deviation ranking and per-sensor reconstruction.

We agree that deviation ranking is a strong reference, and we will add it, together with per-sensor reconstruction using SPARCE's own diffusion model, to Table 1. Deviation ranking scores each sensor by its mean absolute z-score over the window, with the same event aggregation (Eq. 15) as SPARCE. SPARCE leads it by 0.084 to 0.095 R@3 on all four datasets (Table 19).

Per-sensor reconstruction keeps SPARCE's trained model fixed and changes only the attribution procedure: we hide one sensor at a time, reconstruct it conditional on the remaining sensors, and rank sensors by their reconstruction deviation with the same event aggregation. Both use n = 30 restorations: per-sensor reconstruction for every sensor (51 on SWaT, 127 on WADI), SPARCE once per window. Per-sensor values are means over three seeds.

SWaT R@3SWaT CW-RCS@3WADI R@3WADI CW-RCS@3SVAR Root R@1SVAR separation
Per-sensor reconstruction, SPARCE's model0.5280.2520.4280.1550.7240.622
SPARCE (paper)0.6080.3940.4860.3880.8650.768

With the backbone fixed, SPARCE improves R@3 over per-sensor reconstruction by 0.080 on SWaT and 0.058 on WADI, and Root R@1 by 0.141 on SVAR, so the attribution procedure contributes beyond the choice of backbone.

W1 (second part) / Q2. Provenance of baseline numbers and common protocol.

Table 1 valuesSWaT, MSDSWADI, SMD
ε-Diagnosis, RCD, AERCA, KernelSHAP, ShaTS, CondAttrAs reported by Mishra et al. (2026)Our runs
CSDI-RCA, WaveStitch-RCA (our per-sensor adaptation)Our runsOur runs
  • Common protocol. Table 1 follows the evaluation protocol of prior work (Franco De La Peña et al., 2026; Mishra et al., 2026), and the published values are taken from Mishra et al. (2026), who report all these baselines under it. Our runs use the same dataset splits, training-statistic z-score normalization, non-overlapping L = 50 windows, ground-truth anomalous windows, normal training data, VAE detector, event aggregation (Eq. 15), and metric implementations.
  • Implementation and settings. We use official implementations and published hyperparameters, transferring the authors' SWaT settings where a dataset was not covered, without additional baseline tuning (Appendix D). SPARCE's configuration is likewise fixed on SWaT and used unchanged elsewhere, so on WADI, MSDS and SMD no method is tuned for the target dataset.
  • Verification and correction. Our five-seed CondAttr rerun is at or below every Table 1 entry (Table 12), so the reported comparison against CondAttr is conservative relative to our rerun. We will mark each entry's source in the Table 1 caption and correct the corresponding sentence in Appendix E.

W2 / Q3. Learned normal reference, and anchoring versus sparsity.

Q3. We generate 30 restorations once with SPARCE's settings at λm = 0 and reuse them for every window (cached reference; mean ± std over three independent banks).

W2. Anchoring versus sparsity. We replace ℓ1 by a squared ℓ2 term, which anchors to the input without promoting sparsity; λ2 is selected without labels on normal validation windows by matching the mean edit of ℓ1.

SWaT R@3SWaT CW-RCS@3WADI R@3SVAR Root R@1SWaT median edit, non-annotatedSWaT top-3 edit share
Deviation ranking0.5210.2100.3970.4170.5132%
Cached reference (λm = 0, reused)0.526 ± 0.0010.2250.4030.4450.4735%
λm = 0 (Table 3)0.5880.3450.4460.7470.3539%
Squared ℓ2 anchoring0.5940.3670.4700.8120.2943%
ℓ1 (SPARCE)0.6080.3940.4860.8650.2348%
  1. A learned normal reference alone performs at the level of deviation ranking (SWaT R@3 0.526 vs 0.521, SVAR Root R@1 0.445 vs 0.417), far below SPARCE (0.608, 0.865). Subtracting a learned normal reference therefore does not explain SPARCE's performance.
  2. Anchoring and sparsity both contribute. Squared ℓ2 anchoring improves every metric over λm = 0, and ℓ1 adds further gains on every metric and concentrates the edit on fewer sensors (top-3 share 43% → 48%). ℓ1 also stays above the best squared ℓ2 across λ2 from 0.003 to 1.
AuthorsOpenReview ↗

Evidence and clarifications (2/2): role of the detector, theory vs. direct optimization, all-hidden training

W3 / Q6. Role of the detector.

Indeed, SPARCE does not use the detector for attribution. In Tables 1 and 2, the detector is used only to assess restoration validity, i.e. whether the averaged restoration falls below the detector threshold (Table 15).

All ground-truth windows. Tables 1 and 2 already do this: following the protocol of prior work (Franco De La Peña et al., 2026; Mishra et al., 2026), every method attributes all ground-truth anomalous windows (1,059 on SWaT, 194 on WADI), which controls for differences in window selection. We will state this explicitly in Appendix C. Table 16 additionally evaluates the full pipeline, with five detectors (VAE, AE, LSTM, TCN, Transformer) selecting the windows for every method: SPARCE gives the best R@3 in 17 of 20 dataset–detector combinations and the best CW-RCS@3 in 18 of 20.

Comparable detector. Instead of changing the baselines' detector, Table 18 gives SPARCE theirs: the guidance uses the same trained VAE detector that KernelSHAP, ShaTS and CondAttr use, in place of Sθ.

R@3SWaTWADIMSDSSMD
SPARCE, guided by Sθ (Table 1)0.6080.4860.9560.609
SPARCE, guided by the VAE detector0.6120.4810.9660.601
Strongest baseline (CondAttr)0.5370.4620.9480.529

Sharing the baselines' VAE scoring model changes SPARCE's R@3 by at most 0.010, and SPARCE stays ahead on every dataset, so its advantage persists when the scoring model is shared.

W4 / Q4. Theory and the implemented sampler.

We agree that (H3) is not established for the implemented sampler. Theorem A.6 characterizes support recovery conditional on statistical, model and optimization errors; it does not guarantee recovery by SPARCE's averaged output. We will clarify this in the main text and theorem discussion.

Q4. We compared SPARCE with direct optimization in a controlled setting: an exact Gaussian denoiser replaces the network inside the unchanged sampler, and the MAP of the same objective is computed to convergence. G1 has independent entries and G2 temporal AR(1) correlation (ρ = 0.8). Windows are 20 × 50 with unit variance, 100 per setting, with a +2σ fault over 10 steps on s sensors, n = 30 and (λs, λm) = (1, 0.1). Gap = [F(Z) − F(Z_MAP)] / |F(Z_MAP)|, with additive constants omitted; support recall = |Top_s ∩ J*| / s.

SettingsSupport recall: deviation / SPARCE / MAPMedian gap: single draw / averaged
G110.800 / 0.780 / 0.80082% / 3.4%
G120.805 / 0.800 / 0.80593% / 3.8%
G130.827 / 0.830 / 0.833105% / 4.2%
G210.260 / 0.360 / 0.410192% / 8.5%
G220.415 / 0.455 / 0.465190% / 8.4%
G230.460 / 0.557 / 0.573186% / 8.2%
  1. Objective gap: averaging n = 30 draws reduces the median gap to 3.4 to 8.5%, against 82 to 192% for single draws.
  2. Support recovery: in G1, where the prior has no temporal or cross-sensor correlations, the MAP nearly matches deviation ranking and SPARCE stays within 0.02. In G2, SPARCE recovers 67 to 86% of the MAP's gain over deviation ranking.
  3. Minimizer or sampler: single draws carry only 12 to 16% of the target variance (G1, exact quadrature), so the averaged output approximates the objective's minimizer rather than sampling q.

This measures optimization error in a controlled setting; it does not establish H3 for the learned model on real data.

Ratio λs/λm. The reviewer is right (Sec. 4.3, Appendix A): normalized guidance depends only on λs/λm, while the objective and its MAP depend on the absolute weights. The diagnostic therefore evaluates the fixed weights (1, 0.1) used in all our experiments, where the averaged output is within 3.4 to 8.5% of the MAP.

Q5. Training with all-hidden masks.

We ran exactly this, as in conditioning dropout. We retrained with an all-hidden probability p: with probability p all sensors are hidden, otherwise the original 1–3-channel masking is used. Inference is unchanged. Mean ± std over three training seeds:

All-hidden probabilitySWaT R@3WADI R@3Valid % SWaT / WADIAll-hidden loss SWaT / WADI
0% (original)0.608 ± 0.0070.486 ± 0.01081.0 / 67.5%0.150 / 0.175
20%0.614 ± 0.0070.498 ± 0.00682.6 / 70.8%0.133 / 0.152
50%0.611 ± 0.0090.493 ± 0.00882.1 / 69.6%0.128 / 0.146
100%0.595 ± 0.0120.473 ± 0.01279.5 / 65.9%0.124 / 0.141

All-hidden loss is the held-out denoising loss with every sensor hidden (lower is better). It keeps falling with more all-hidden training, while R@3 peaks at 20% and is lowest at 100%. All settings stay within 0.013 R@3 of the original, and we will add this ablation to the supplement.

We hope our responses resolve the reviewer’s concerns. If so, we would appreciate it if the reviewer would consider updating the score. We are happy to answer any further questions.

AuthorsOpenReview ↗

Follow-up on our response

As the discussion period ends on 18 November, we wanted to ask whether our response addresses your concerns. The revised PDF includes deviation ranking and per-sensor reconstruction with SPARCE’s model as new rows in Table 1, the source of each Table 1 entry in its caption, the explicit use of all ground-truth windows in Appendix C, and the clarified scope of the theorem in Section 3.3.

If our response and these revisions resolve your concerns, we would be grateful if you would consider increasing your rating. We welcome any remaining questions while there is still time to answer them.

Reviewer_r9oeOpenReview ↗
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3
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2
Informativeness
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3
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Paper summary

The paper frames a root cause analysis in multivariate time series as a sparse counterfactual restoration problem. I am not an expert in the area but the basic idea seems very clever - i.e. identifying the sensors responsible for an anomaly can be framed as finding the minimal sparse edit to an anomalous window that restores it to the normal data manifold.

Critical strengths

The paper is very well written and easy to follow.

Critical weaknesses

None

Questions for authors

What is the justification for Equation (2). I could not follow this. Also, the comment on "independence" was v very difficult to follow.

3 comments
AuthorsOpenReview ↗

Clarification of Eq. (2) and the independence assumption

We thank the reviewer for the positive assessment and for raising two points that need clarification.

Q1. Justification of Equation (2).

Eq. (2) says that an anomalous window equals what the system would normally have shown, plus a change on a few sensors. Root cause analysis then means finding which sensors carry that change. Any window can be written as a normal reference plus a difference; the assumption is that this difference affects only a few sensors.

Formally, W_anom = W^N + D*, where D* is non-zero on a small set of sensors J(D*). This follows the structured-plus-sparse principle of robust PCA (Candès et al., 2011), with normal behaviour given by a learned distribution instead of a low-rank model. When a fault propagates, J(D*) also contains the downstream sensors it affects. We will add this explanation directly after Eq. (2).

Q2. The comment on independence.

SPARCE asks which normal window, changed on a few sensors, best explains the observed one. Before seeing the data, it treats "what normal behaviour looks like" and "where the change is" as two separate questions; once the anomalous window is observed, the answers are tied together. This does not mean that sensors are treated as independent: the learned normal model captures temporal and cross-sensor dependencies.

Formally, the prior of the inference model factorizes as p(Z, D) = p_N(Z) π(D), with an entrywise Laplace prior π on the edit, which gives the ℓ1 penalty (Park & Casella, 2008); conditioning on W_anom = Z + D gives Eq. (4). This is a modeling choice for inference only: the recovery result (Theorem A.6) requires neither that the true fault be independent of normal behaviour nor that it follow a Laplace distribution. We will make this distinction explicit in Section 3.

We hope these clarifications further strengthen the reviewer's positive assessment, and we would be happy to answer any further questions.

References:

Candès, E. J., Li, X., Ma, Y., and Wright, J. (2011). Robust principal component analysis? Journal of the ACM, 58(3), Article 11.

Park, T. and Casella, G. (2008). The Bayesian Lasso. Journal of the American Statistical Association, 103(482), 681–686.

Thank you for the clarification

AuthorsOpenReview ↗

Clarifications added to the revised PDF

Thank you for reading our response. We have incorporated both clarifications into the revised PDF: the explanation immediately after Eq. (2), and the distinction between the inference-model independence assumption and the true fault process in Section 3.

If these clarifications resolve your questions, we would be grateful if you would consider increasing your rating.

Reviewer_9HwpOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
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Paper summary

The paper targets root cause analysis (RCA) in multivariate time-series anomaly detection: not merely whether a fault occurred but which sensors are responsible. Its key observation is that identifying responsible sensors can be recast as finding the minimal sparse edit to an anomalous window that restores it to the normal data manifold. Existing attribution methods — marginal feature perturbation (KernelSHAP, CondAttr) and finite nearest-neighbor retrieval (ShaTS) — produce out-of-distribution counterfactuals that violate the conditional dependencies of real monitoring systems, so their attributions reflect single-sensor sensitivity rather than the joint, system-consistent edit.

SPARCE approximates the minimal-edit problem by injecting gradient-based guidance into the reverse process of a conditional score-based diffusion model trained exclusively on normal behavior. At each denoising step, guidance jointly optimizes a denoising-consistency regularizer (pull toward normal) and an L1 sparsity penalty (concentrate the edit). The attribution map is the pointwise difference between the anomalous input and the diffusion-restored output, so all sensors are attributed in a single pass — no per-sensor enumeration, no detector queries. On SWaT, WADI, MSDS and SMD the method improves Recall@K, CW-RCS and TemporalHM over strong baselines, with two decisive design choices: normalizing the guidance gradient, and guiding only the high-noise half of the reverse process.

Critical strengths

Recasting RCA as minimal sparse counterfactual restoration is a real problem reformulation — it converts a ranking heuristic into an explicit inference objective — and the single-pass gradient-guided diffusion realizes it with strong, honestly reported gains, including an external-detector validity check.

  1. Sharp problem formulation. Recasting RCA as minimal sparse counterfactual restoration converts a ranking heuristic into an explicit inference objective, and the paper is unusually candid about the scope and recovery conditions of that objective. This is the paper's central and strongest contribution.
  2. The OOD-counterfactual critique is correct and well-argued. Marginal perturbation breaks inter-sensor dependencies; nearest-neighbor retrieval is sample-starved. Framing the failure as "OOD counterfactuals" is precise and motivating.
  3. Clean, well-motivated design. Gradient-guided reverse diffusion with a joint consistency + L1 objective is a natural fit; a sparsity prior yields concentrated edits (§4.4), and the ablation shows guidance is necessary (no guidance R@3 0.484 vs 0.608 full) and that gradient normalization is decisive (Top-3 Recall on SWaT collapses 0.608 → 0.044 without it).
  4. Strong and honest evidence. Best Recall@3 on all four datasets and best/tied Recall@5; +13.2% Recall@3 on SWaT and +15.1% on SMD over the strongest baseline. Crucially, restorations pass an external detector they were never optimized against (replacing the surrogate changes Recall@3 by ≤0.010), which is a good validity check. Matched-aggregation (Table 4) shows the ordering is not an aggregation artifact.
  5. Synthetic intervention benchmark genuinely informative. On Structural-VAR with known intervention targets, the same readout recovers initiating faults (Root Recall@1 0.865 vs 0.417 for deviation ranking; Multi-root R@2 0.728 vs 0.080) — a qualitative capability that deviation ranking lacks.
  6. Efficiency analysis. ~20 s/window on SWaT (comparable to baselines) and ~3.5× faster on WADI (20.3 s vs 71.3 s/window).
  7. Robustness checks. Small sensitivity to η/λm/n, 17/20 best across five detector backbones, modest degradation under 40% synthetic training contamination.
Critical weaknesses

The distinctive capability that motivates the reformulation — separating initiating faults from downstream propagation — is demonstrated only on a synthetic benchmark, and the restoration objective is approximated without any sampling or optimality guarantee.

  1. Separating initiating faults from propagation is solved only on synthetic data. The authors explicitly concede that under fault propagation the edited set also contains downstream sensors, and that separating initiating faults is evaluated only on the synthetic Structural-VAR benchmark. This is precisely the hard, high-value part of RCA in real systems; the headline "root cause" claim is therefore supported mainly in a controlled setting.
  2. The restoration objective is only approximated. The guided sampler approximates Eq. (7) with no guarantee of sampling it or reaching its mode (acknowledged). Hence the "minimal sparse edit" optimality is nominal; the sparsity/consistency trade-off is controlled by hyperparameters with no bound on restoration correctness.
  3. Attribution inherits the normal prior and degrades with it. Under training contamination or distribution shift the prior — and thus the attribution — degrades. "Train on normal only" often fails in practice (unlabeled anomalies leak in); the 40% synthetic-contamination result helps but synthetic contamination is structurally different from real leakage.
  4. Sparse prior can under-count multi-root faults. L1 sparsity assumes few responsible sensors; genuine multi-sensor co-faults would be systematically under-attributed. Multi-root is tested only synthetically (R@2 0.728).
  5. Continuous diffusion is mismatched to discrete sensors. Binary/categorical sensors are poorly handled (Austin et al., 2021, acknowledged); industrial telemetry is full of switches and mode variables, yet no discrete/mixed-diffusion extension is offered.
  6. Metric saturation on MSDS. With only 10 metrics, Recall@5 saturates and comparisons lose discriminative power; the paper leans on CW-RCS/TemporalHM but the headline remains Recall@K.
  7. Baseline reproduction inconsistency. Coverage is otherwise adequate (feature attribution, nearest-neighbor, causal-discovery methods, conditional attribution, and CSDI/WaveStitch diffusion baselines), but the appendix notes that CondAttr's rerun falls slightly below its published values while Table 1 retains the published values. The "strongest baseline" is therefore taken from a different measurement protocol than the authors' own rerun, which directly affects the interpretation of the +13.2% / +15.1% margins.
  8. Absolute latency. ~20 s/window, ~354 min for all SWaT attack windows, is heavy for online RCA; the paper argues relative speed but not absolute deployability or streaming.
  9. Homogeneous datasets. All four are industrial/water/server; no medical, traffic, or energy settings with different sensor semantics and so on.
Questions for authors
  1. Can you provide any evidence — that the edited set corresponds to initiating faults (not propagation) on a real, non-synthetic benchmark, or a rigorous argument for why the Structural-VAR result transfers?
  2. How sensitive is root attribution to the L1 weight λ and to the number of truly responsible sensors? Can you characterize the failure mode for multi-root faults?
  3. Given the sampler only approximates Eq. (7), what would constitute a correctness certificate for a restoration (e.g., detector-validity + edit-concentration thresholds)? Do you have a principled stopping criterion?
  4. How does the method behave when the "normal-only" training set contains real, systemically correlated (not synthetic) contamination or shift?
  5. Is there any plan to handle binary/categorical sensors (discrete or mixed diffusion)?
  6. Please clarify the CondAttr reproduction discrepancy: were baselines tuned with comparable budgets, and how would the margin change under matched tuning?
  7. In the real SWaT/WADI/SMD settings, what fraction of ground-truth RCA labels (if any) correspond to initiating faults, and how is precision measured?
4 comments
AuthorsOpenReview ↗

Evidence and clarifications (1/2): directly attacked sensors on real data, objective gap vs. direct optimization, reliability check, real training contamination

We thank the reviewer for the thorough review and for recognizing the sharp problem formulation, the critique of out-of-distribution counterfactuals, the clean design and the strong, honestly reported evidence. We provide new experiments and clarifications below.

W1 / Q1 / Q7. Initiating faults on real data.

We agree that the paper demonstrates initiating-fault separation only on Structural-VAR. We now add real-data evidence on SWaT and WADI. We use the documented attack descriptions to identify directly attacked sensors J_att, excluding sensors affected only through propagation; these are the real-world counterpart of the Structural-VAR intervention targets.

Q7. Of the sensor annotations across events, 87% on SWaT and 88% on WADI are directly attacked sensors, and every event has at least one. SMD's labels do not document intervention locations, so the fraction cannot be determined there. We will revise the label description in Appendix C.

Q1. We score the existing rankings against J_att, without retraining: Recall@3 = |Top₃ ∩ J_att| / min(3, |J_att|) and Precision@3 = |Top₃ ∩ J_att| / 3. Precision@3 cannot reach 1 when an event has fewer than three directly attacked sensors; its maximum here is 0.43 (SWaT) and 0.51 (WADI).

Directly attacked sensors: R@3 / P@3SWaTWADI
Deviation ranking0.417 / 0.2310.361 / 0.267
CondAttr0.629 / 0.2260.472 / 0.222
SPARCE0.693 / 0.3150.694 / 0.385

On directly attacked sensors, SPARCE exceeds both deviation ranking and CondAttr in recall and precision on both datasets.

W2 / Q3. Approximate objective and a correctness certificate.

As stated in our limitations, the guided sampler approximates Eq. (7) without a guarantee of sampling it or reaching its mode. To measure how far it is from the optimum of this objective, we placed an exact Gaussian denoiser inside the unchanged sampler and computed the MAP of the same objective to convergence (20 × 50 windows, 100 per setting, a +2σ fault on 1 to 3 sensors, n = 30, (λs, λm) = (1, 0.1)). Gap = [F(Z) − F(Z_MAP)] / |F(Z_MAP)|, with additive constants omitted.

Median relative gap to the MAP objective valueIndependent priorTemporally correlated prior (AR(1), ρ = 0.8)
Single draw82 to 105%186 to 192%
SPARCE (average of n = 30 draws)3.4 to 4.2%8.2 to 8.5%
  • Close to the optimum: single draws are far from the optimum, but SPARCE's averaged output is within 3.4 to 8.5% of it.
  • Trade-off not fragile: λm = 0.1 is best for one, two and three roots, and the largest drop across the tested range is 0.049 R@r (W4/Q2).

Q3, certificate. Following the reviewer's suggestion, we combined detector validity with edit concentration (share of edit mass on the top three sensors), both label-free; high concentration is the top tertile of each dataset's windows.

Hit rate (≥ 1 annotated sensor in top 3)SWaTWADI
All windows0.700.59
Valid and high concentration (28% / 26% of windows)0.860.94
Invalid0.550.48

Concentration alone predicts a hit with AUROC 0.70 (SWaT) and 0.83 (WADI). Windows passing both checks contain an annotated sensor in their top three far more often, and failing windows can be flagged for review; this is an empirical acceptance test, not a guarantee.

Q3, stopping criterion. We do not have a principled adaptive stopping rule; inference uses a fixed schedule (T = 50, guidance in the high-noise half, n = 30), whose sensitivity is reported in Tables 20 and 21.

W3 / Q4. Real contamination of the training data.

We repeated the contamination study with real leakage. SWaT attack events are split with a fixed seed into a contamination pool (10 events) and an evaluation set (the remaining 26). Windows from the pool are added to the normal training split at 5 to 20% of its size (112 distinct attack windows, repeated as needed), the model is retrained at each level, and attribution is evaluated on the 26 held-out events. Real attack windows keep their temporal and cross-sensor structure, and pool and evaluation events share attacked sensors (e.g., LIT-101), so the model is trained on anomalous behaviour of sensors it must later attribute.

Attack windows added (% of normal training size)0%5%10%20%
R@30.6350.6300.6240.609
CW-RCS@30.4520.4480.4420.431
S_θ ROC-AUC0.9420.9320.9160.883

On the same held-out events, 20% real contamination reduces R@3 by 0.026 and CW-RCS@3 by 0.021, a gradual degradation. As the reviewer anticipated, real leakage costs more than synthetic faults at a comparable level (−0.004 R@3 at 20%, Table 17); as there, attribution degrades more slowly than the normality score.

AuthorsOpenReview ↗

Evidence and clarifications (2/2): multi-root faults on real data, discrete sensors, CondAttr rerun, latency

W4 / Q2. Sensitivity to λm and multi-root faults.

On Structural-VAR we injected one, two and three simultaneous roots (200 windows each, three seeds) and varied λm. R@r = |Top_r ∩ roots| / r; separation is the fraction of roots ranked above all their direct children, reported per root count (the paper's 0.768 pools one and two roots).

RootsR@r at λm = 0.03 / 0.1 / 0.3Separation (λm = 0.1)Deviation ranking R@r
10.839 / 0.865 / 0.8310.7890.417
20.694 / 0.728 / 0.6810.7570.080
30.604 / 0.631 / 0.5820.7180.113
  • Sensitivity to λm is low: λm = 0.1 is best for every root count, and across the tested range the largest drop is 0.049. A stronger ℓ1 weight (λm = 0.3) costs slightly more on three roots than on one (0.049 vs 0.034).
  • Number of roots: multi-root faults become harder but are not collapsed onto one sensor: with three roots, SPARCE recovers on average 1.89 of them in its top three.
  • Real data: events with two or more directly attacked sensors are real multi-sensor co-faults. On them, SPARCE reaches R@3 0.669 (SWaT) and 0.620 (WADI) on directly attacked sensors, close to its 0.693 and 0.694 over all events (W1/Q1).
  • Failure mode: separation declines from 0.789 to 0.718; as roots multiply, they are more often outranked by their own downstream children.

W5 / Q5. Discrete sensors.

This is a limitation, and we quantified it. SWaT has 26 discrete actuators among 51 channels and WADI 31 among 127. Grouping events by the type of their annotated sensors:

R@3Deviation rankingSPARCESPARCE + snapping
SWaT, discrete-only events (8)0.3150.4000.430
SWaT, all events (36)0.5210.6080.620
WADI, discrete-only events (7)0.2900.4000.435
WADI, all events (15)0.3970.4860.507

Discrete-only events are harder (0.400 against 0.694 for continuous-only events on SWaT), but SPARCE still exceeds deviation ranking on them. Snapping each discrete channel of the averaged restoration W* to the nearest state observed in normal training data, before the readout, recovers part of the gap without retraining or anomaly labels.

Q5. Yes: mixed continuous–discrete diffusion is the principled extension and our planned future work; snapping is a simple inference-time mitigation until then.

W6. Saturation on MSDS.

We agree: on MSDS, Recall@5 saturates at 1.000 for SPARCE and CondAttr, and we will state this explicitly. CW-RCS@3 still separates them (0.595 vs 0.551, Table 13), and the headline Recall gains come from SWaT (+13.2%) and SMD (+15.1%).

W7 / Q6. CondAttr reproduction and tuning budget.

  • Discrepancy. Our five-seed CondAttr rerun (Table 12) is at or below every Table 1 CondAttr entry, by at most 0.014 R@3 (SWaT: 0.537 vs 0.523). Table 1 keeps the stronger values (published on SWaT and MSDS, our single runs on WADI and SMD), so its margins are conservative: against the rerun, SPARCE's R@3 gain is +16.3% on SWaT and +15.6% on SMD, versus +13.2% and +15.1% in Table 1. We will mark each entry's source in the Table 1 caption.
  • Common protocol. All methods use the same splits, windows, VAE detector, event aggregation and metric implementations, following prior work (Franco De La Peña et al., 2026; Mishra et al., 2026).
  • Tuning budget. Baselines use their authors' published hyperparameters, with their SWaT settings where a dataset was not covered; SPARCE's configuration is fixed on SWaT and used unchanged elsewhere. On WADI, MSDS and SMD, every method therefore has the same tuning budget for the target dataset: none. In Table 12, every non-tied Recall comparison favours SPARCE at p < 0.01.

W8. Absolute latency.

We agree that about 20 s per window at batch size 1 (n = 30) is heavy for time-critical online RCA.

  • Batching: for a single window, running all n = 30 restorations in one pass cuts latency on SWaT from 20.0 to 2.8 s. For throughput, batching 35 (SWaT) or 30 (WADI) windows gives an amortized 3.0 s and 6.3 s per window, with the same attribution procedure.
  • Sensor count: from SWaT to WADI (51 → 127 sensors), SPARCE's time per window rises only from 20.0 to 20.3 s, while ShaTS and CondAttr slow down 3.3× (Table 7), so SPARCE's advantage grows with the number of sensors.

W9. Dataset diversity.

Evaluation is indeed limited to industrial and IT monitoring, using public benchmarks with sensor-level annotations. They still cover distinct sensor semantics: physical processes with sensors and actuators (SWaT, WADI) and computing infrastructure with resource metrics (MSDS, SMD), plus known interventions on Structural-VAR. SPARCE needs only normal training data, so it can be applied to other domains as annotated benchmarks appear; we will state this limitation explicitly.

We hope these experiments and clarifications further strengthen the reviewer's positive assessment, and we would be happy to answer any further questions.

AuthorsOpenReview ↗

Follow-up on our response

As the discussion period ends on 18 November, we wanted to ask whether our response addresses your concerns. The revised PDF includes the revised label description in Appendix C and the source of each Table 1 entry in its caption.

If our response and these revisions resolve your concerns, we would be grateful if you would consider increasing your rating. We welcome any remaining questions while there is still time to answer them.

Thank you for your detailed reply, which has answered my questions. I choose to keep my rating.

Reviewer_3b2sOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes SPARCE, a root-cause attribution method for multivariate time-series anomalies.The main idea is to formulate attribution as sparse counterfactual restoration. For the anomalous window, It seeks a nearby window that is compatible with the learned distribution of normal system behavior, and attributes the anomaly to sensors requiring the largest edits. Experiments covers four real-world benchmarks valid its improvements on Recall@K and TemporalHM.The paper also provides component ablations, matched aggregation, robustness and latency analyses, restoration diagnostics, and a synthetic Structural-VAR experiment with known intervention targets.

Critical strengths

1 The formulation is well-motivated. Framing attribution as sparse restoration under a learned normal prior is intuitive and better aligned with strongly coupled monitoring systems than independently perturbing or reconstructing each sensor. 2.The broad empirical analysis is strong. The evaluation covers four real-world benchmarks and multiple classes of baselines. The matched-aggregation experiment is also useful because it reduces the possibility that the gains arise solely from the proposed event-level readout. 3.Careful discussion of scope and theoretical limitations.The paper explicitly distinguishes observable deviations from initiating physical faults. It also clearly states that the support-recovery theorem applies to approximate minimizers of the stated objective. This transparency is valuable.

Critical weaknesses

1.During training, only one to three sensor channels are hidden, whereas inference uses the all-hidden configuration, which has zero probability under the training masking distribution. Consequently, the model is trained for conditional reconstruction but used as an unconditional joint score model without direct training for that mode. 2.The support-recovery theorem assumes that the output approximately minimizes the proposed objective, but the paper does not show that SPARCE satisfies this assumption. 3.SPARCE avoids per-sensor enumeration, but it is not a single inference pass in the ordinary computational sense.The latency comparison includes only a subset of baselines and does not report memory consumption or scaling with window length and sensor count. The method may scale better with the number of sensors, but its absolute inference cost remains high for online RCA. 4.The abstract and introduction are occasionally overly dense. For example, the sentence beginning “SPARCE attributes observable deviations...” compresses several distinct claims—fault propagation, downstream-sensor attribution, and detector agnosticism—without sufficient transitions or explanation. This requires readers to process multiple new concepts simultaneously and reduces readability.

Questions for authors

The support-recovery result assumes that the estimated edit approximately minimizes the proposed objective, but the paper does not establish this condition for the guided sampler or the averaged restoration. Can the authors empirically measure the objective gap of SPARCE’s output, for example by comparing it with a direct optimization baseline? More generally, what evidence indicates that the implemented sampler approximates either a mode or representative sample of the stated target distribution?

3 comments
AuthorsOpenReview ↗

Evidence and clarifications: all-hidden training, objective gap vs. direct optimization, full latency comparison

We thank the reviewer for the careful reading and for recognizing the formulation, the breadth of the evaluation and the transparent discussion of scope and theory. We provide new experiments and clarifications below.

W1. All-hidden mode is never trained.

Yes, hiding 1 to 3 channels never produces the all-hidden configuration used at attribution. We therefore retrained with an all-hidden probability p: with probability p all sensors are hidden, otherwise the original 1–3-channel masking is used. Inference is unchanged. Mean ± std over three training seeds:

All-hidden probabilitySWaT R@3WADI R@3Valid % SWaT / WADIAll-hidden loss SWaT / WADI
0% (original)0.608 ± 0.0070.486 ± 0.01081.0 / 67.5%0.150 / 0.175
20%0.614 ± 0.0070.498 ± 0.00682.6 / 70.8%0.133 / 0.152
50%0.611 ± 0.0090.493 ± 0.00882.1 / 69.6%0.128 / 0.146
100%0.595 ± 0.0120.473 ± 0.01279.5 / 65.9%0.124 / 0.141

All-hidden loss is the held-out denoising loss with every sensor hidden (lower is better). It keeps falling with more all-hidden training, while R@3 peaks at 20% and is lowest at 100%. All settings stay within 0.013 R@3 of the original, and we will add this ablation to the supplement.

W2 / Question. The theorem's optimization assumption.

We agree that (H3) is not established for the implemented sampler. Theorem A.6 characterizes support recovery conditional on statistical, model and optimization errors; it does not guarantee recovery by SPARCE's averaged output. We will clarify this in the main text and theorem discussion.

Following the reviewer's suggestion, we compared SPARCE with direct optimization in a controlled setting: an exact Gaussian denoiser replaces the network inside the unchanged sampler, and the MAP of the same objective is computed to convergence. G1 has independent entries and G2 temporal AR(1) correlation (ρ = 0.8). Windows are 20 × 50 with unit variance, 100 per setting, with a +2σ fault over 10 steps on s sensors, n = 30 and (λs, λm) = (1, 0.1). Gap = [F(Z) − F(Z_MAP)] / |F(Z_MAP)|, with additive constants omitted; support recall = |Top_s ∩ J*| / s.

SettingsSupport recall: deviation / SPARCE / MAPMedian gap: single draw / averaged
G110.800 / 0.780 / 0.80082% / 3.4%
G120.805 / 0.800 / 0.80593% / 3.8%
G130.827 / 0.830 / 0.833105% / 4.2%
G210.260 / 0.360 / 0.410192% / 8.5%
G220.415 / 0.455 / 0.465190% / 8.4%
G230.460 / 0.557 / 0.573186% / 8.2%
  1. Objective gap: averaging n = 30 draws reduces the median gap to 3.4 to 8.5%, against 82 to 192% for single draws.
  2. Support recovery: in G1, where the prior has no temporal or cross-sensor correlations, the MAP nearly matches deviation ranking and SPARCE stays within 0.02. In G2, SPARCE recovers 67 to 86% of the MAP's gain over deviation ranking.
  3. Minimizer or sampler: single draws carry only 12 to 16% of the target variance (G1, exact quadrature), so the averaged output approximates the objective's minimizer rather than sampling q.

This measures optimization error in a controlled setting; it does not establish H3 for the learned model on real data.

W3. Computational cost.

We agree that SPARCE runs n reverse trajectories rather than one pass, and that its per-window cost is still high for time-critical online use. What it avoids is one pass per sensor. Latency at batch size 1 on one RTX A6000, extending Table 7:

MethodSWaT (51 sensors, 1,059 windows): s/window / total minWADI (127 sensors, 194 windows): s/window / total min
KernelSHAP18.7 / 32968.7 / 222
ShaTS21.8 / 38571.3 / 231
CondAttr22.0 / 38871.6 / 232
CSDI-RCA100.1 / 1,766400.1 / 1,294
WaveStitch-RCA101.0 / 1,783400.2 / 1,294
SPARCE20.0 / 35420.3 / 66
  • Batching: for a single window, running all n = 30 restorations in one pass cuts latency on SWaT from 20.0 to 2.8 s. For throughput, batching 35 (SWaT) or 30 (WADI) windows gives an amortized 3.0 s and 6.3 s per window, with the same attribution procedure.
  • Sensor count: from SWaT to WADI (51 → 127 sensors), SPARCE's time per window rises from 20.0 to 20.3 s, while the five baselines slow down 3.3 to 4.0×.
  • Window length: for L from 25 to 100, latency stays at 20.1 to 20.3 s, and peak GPU memory grows from 0.08 to 0.28 GB. Peak memory stays below 0.7 GB at batch 1 for up to 250 sensors.

W4. Dense abstract and introduction.

Thank you for this suggestion. In the revised PDF, we have rewritten the abstract and introduction so that each sentence introduces one idea. The sentence the reviewer quotes is now split into three shorter sentences.

We hope these experiments and clarifications further strengthen the reviewer's positive assessment, and we would be happy to answer any further questions.

AuthorsOpenReview ↗

Follow-up on our response

As the discussion period ends on 18 November, we wanted to ask whether our response addresses your concerns. The revised PDF includes the rewritten abstract and introduction and the clarified scope of the theorem in Section 3.3.

If our response and these revisions resolve your concerns, we would be grateful if you would consider increasing your rating. We welcome any remaining questions while there is still time to answer them.

Thanks for your clarification. I choose to retain my rank.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of the discussion for the AC

We thank the AC and all reviewers for their time and constructive feedback. Summary of the discussion:

  • 3b2s, 9Hwp, r9oe: we addressed all questions; reviewers acknowledged the clarifications, which are now in the revised PDF.
  • BJAo: acknowledged that several concerns were addressed; our follow-up answers the three remaining concerns:
    1. Cached vs. fresh gap: explained as an effect of reference dependence under event aggregation, not of the diffusion model; independent references per window recover 83% of it. SPARCE's input-dependent guidance is what raises window-level R@3 (.442 → .491), and it is significant over the input-independent reference on every dataset.
    2. ℓ1 vs. ℓ2: five-seed ablation on all four datasets, Holm-corrected. All 32 differences favour ℓ1; ℓ1 is significant over no penalty in 14/16 comparisons and over ℓ2 in 9/16.
    3. Scope of Theorem A.6: a controlled Gaussian experiment shows the sampler approximately minimizes the objective (3.4-8.5% gap after averaging); the theorem's scope is now stated as a limitation in Section 5.4.
  • Correction: the cached-reference experiment in our first response to BJAo had readout and normalization errors; corrected values are in the follow-up. No result in the paper, in other experiments, or in our responses to other reviewers is affected.
  • Revised PDF: includes the requested changes, with the new Table 1 baselines and the full ablations in Appendix E.12 and E.13.

We are grateful for the reviewers’ engagement, which helped us strengthen the evidence and sharpen the paper’s claims. We believe the revised paper and additional analyses address the concerns raised.

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

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