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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 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
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@3 | SWaT | WADI | MSDS | SMD |
|---|---|---|---|---|
| SPARCE, guided by Sθ (Table 1) | 0.608 | 0.486 | 0.956 | 0.609 |
| SPARCE, guided by the VAE detector | 0.612 | 0.481 | 0.966 | 0.601 |
| Strongest baseline (CondAttr) | 0.537 | 0.462 | 0.948 | 0.529 |
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.
| Setting | s | Support recall: deviation / SPARCE / MAP | Median gap: single draw / averaged |
|---|---|---|---|
| G1 | 1 | 0.800 / 0.780 / 0.800 | 82% / 3.4% |
| G1 | 2 | 0.805 / 0.800 / 0.805 | 93% / 3.8% |
| G1 | 3 | 0.827 / 0.830 / 0.833 | 105% / 4.2% |
| G2 | 1 | 0.260 / 0.360 / 0.410 | 192% / 8.5% |
| G2 | 2 | 0.415 / 0.455 / 0.465 | 190% / 8.4% |
| G2 | 3 | 0.460 / 0.557 / 0.573 | 186% / 8.2% |
- Objective gap: averaging n = 30 draws reduces the median gap to 3.4 to 8.5%, against 82 to 192% for single draws.
- 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.
- 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 probability | SWaT R@3 | WADI R@3 | Valid % SWaT / WADI | All-hidden loss SWaT / WADI |
|---|---|---|---|---|
| 0% (original) | 0.608 ± 0.007 | 0.486 ± 0.010 | 81.0 / 67.5% | 0.150 / 0.175 |
| 20% | 0.614 ± 0.007 | 0.498 ± 0.006 | 82.6 / 70.8% | 0.133 / 0.152 |
| 50% | 0.611 ± 0.009 | 0.493 ± 0.008 | 82.1 / 69.6% | 0.128 / 0.146 |
| 100% | 0.595 ± 0.012 | 0.473 ± 0.012 | 79.5 / 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.
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.
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.
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.
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.