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Under review as a conference paper at ICLR 2027

Anomaly Localization as a Defense Against Sensor Faults in Virtual Sensing

Abstract

Learning-based virtual sensors inherit the vulnerability of the physical sensors they consume. When a transducer drifts, saturates, or sticks, the input distribution shifts and predictions degrade. We tackle this with a detect–isolate–accommodate pipeline, in which a fault detector flags and discards failing sensors before they reach the predictor. This shifts the burden from learning invariance across the full fault manifold to recognizing departures from normality, collapsing the predictor's necessary training augmentation to plain channel dropout. To make this pipeline work, what matters is not only when a channel misbehaves but which one does. Yet time-series anomaly detectors are built and benchmarked almost exclusively for the former. We test whether they can serve as channel-level isolators end-to-end on a benchmark for sensor-failure robustness in virtual sensing, spanning six domains, nine datasets and ten failure modes. Finding that current state-of-the-art detectors localize faulty channels poorly, we propose itx, an iTransformer adaptation with untied per-channel embeddings and projections, trained with cross-instance channel substitution to simulate plausible-but-wrong sensor readings. It substantially improves channel-level localization and, paired with a dropout-trained back-end, makes explicit fault isolation the best-ranked robustification in our evaluation.

Primary area:
learning on time series and dynamical systems
Keywords:
virtual sensing, time-series anomaly detection, anomaly localization, sensor fault isolation, multivariate time series

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
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Paper summary

The paper casts sensor-fault robustness of learned virtual sensors as a detect–isolate–accommodate pipeline: an anomaly detector flags faulty input channels, which are zeroed before a ModernTCN predictor trained with random input-channel dropout. Finding that recent time-series anomaly detectors (CATCH, CrossAD, ALoRa) localize faulty channels poorly, it proposes ITX, an iTransformer reconstruction model with untied per-channel embeddings/heads and no instance normalization, trained to recover clean windows after random channels are swapped with those of other batch samples. On the MuViS-C benchmark (nine datasets, ten synthetic single-channel failure modes), ITX gives the best channel localization and, as a gate, the best mean rank against MuViS-C's robustified baselines, with a supplementary localization check on SMD.

Critical strengths
  • The one genuinely new contribution is empirical: a benchmark-scale test of modern anomaly detectors as channel isolators, scored both by which channel they flag and by a downstream virtual sensor's error between naive and oracle gates, which shows a per-channel 3σ chart ranking ahead of CATCH, CrossAD and ALoRa (Table 2). It is new evidence rather than a new idea, since simple baselines are known to rival deep detectors [1] and Fu & Yan already evaluated a sensor fault-isolation pipeline by a downstream estimator's error [2].
  • The paper is clearly written: the pipeline, isolation protocol and metrics are precisely specified, and the appendices candidly report per-mode and per-severity results, false-alarm costs on clean data, test-set capping, and the upper-bound nature of the SMD protocol, with code released.

References

  • [1] M. S. Sarfraz et al. Position: Quo Vadis, Unsupervised Time Series Anomaly Detection? ICML 2024, PMLR 235:43461–43476.
  • [2] Y. Fu and W. Yan. One Masked Model is All You Need for Sensor Fault Detection, Isolation and Accommodation. IJCNN 2024 (arXiv:2403.16153).
Critical weaknesses
  • ITX's key ingredients are established yet uncited: cross-instance substitution is VIME's marginal-resampling corruption, motivated the same way (harder to spot than zeros or noise) [3] and also used by SCARF [4]; per-sensor embeddings with per-sensor deviation scores are central to GDN [5]; and validating inputs before a virtual sensor dates to self-validating inferential sensors [6]. No close isolator (leave-one-channel-out masking [2], PCA reconstruction-based validation [7, 8]) or repair-type defense is run, and CATCH [9] keeps its RevIN layer [10], which by construction hides constant-bias and stuck-at faults (Table 12: near-Naive on both) — the very property the authors invoke to remove RevIN from ITX.
  • The "best-ranked robustification" claim is confounded: the ITX gate feeds a dropout-trained ModernTCN whereas MuViS-C hardens only a TST backbone [11]; about 40% of ITX's geometric-mean edge over XGBoost and CatBoost (Table 2) comes from HR, where an undefended ModernTCN already matches it (mPC 5.27 vs 5.30); and rPC rewards the gated system's inflated clean error (HR clean RMSE 3.53 vs ≈2.41 for the undefended ModernTCN). What remains is modest and not significant: against the best existing model per dataset, ITX wins clearly only on Vehicle (−27% mPC) and MMR (≈−13%), so its lead reflects consistency rather than large gains, and it is Nemenyi-significant only over bottom-ranked models, with PM10 and PM2.5 (identical detector results, implying shared inputs) counted as separate datasets and a mean-rank test whose outcomes depend on the pool [12].
  • The evidence for ITX's design and generality is thin: all results come from a single training seed; the cumulative single-seed ablation on three dataset subsets attributes most of the recall gain to per-channel embeddings/heads and gives mixed support for substitution (no precision/recall gain over plain reconstruction on Vehicle; lower REVS precision than zero-masking); and the SMD check uses one machine with test-label thresholds where ITX trails ALoRa on 4 of 6 localization metrics. The evaluation also departs from deployment: test-time operating points are unmatched (Table 1 implies ≈0% healthy-channel false positives on Battery for 3σ/CATCH/CrossAD versus ≈9% for ITX), and every evaluated window contains exactly one fault, so the clean-data cost of gating is never weighed against realistic fault prevalence (on PM2.5, gating adds 3.3% clean RMSE in Table 13 for only a 3.5% mPC reduction in Table 2).

References

  • [3] J. Yoon, Y. Zhang, J. Jordon, and M. van der Schaar. VIME: Extending the Success of Self- and Semi-supervised Learning to Tabular Domain. NeurIPS 2020.
  • [4] D. Bahri, H. Jiang, Y. Tay, and D. Metzler. SCARF: Self-Supervised Contrastive Learning using Random Feature Corruption. ICLR 2022.
  • [5] A. Deng and B. Hooi. Graph Neural Network-Based Anomaly Detection in Multivariate Time Series. AAAI 2021, 35(5):4027–4035.
  • [6] S. J. Qin, H. Yue, and R. Dunia. Self-Validating Inferential Sensors with Application to Air Emission Monitoring. Industrial & Engineering Chemistry Research, 36(5):1675–1685, 1997.
  • [7] R. Dunia, S. J. Qin, T. F. Edgar, and T. J. McAvoy. Identification of Faulty Sensors Using Principal Component Analysis. AIChE Journal, 42(10):2797–2812, 1996.
  • [8] C. F. Alcala and S. J. Qin. Reconstruction-Based Contribution for Process Monitoring. Automatica, 45(7):1593–1600, 2009.
  • [9] X. Wu et al. CATCH: Channel-Aware Multivariate Time Series Anomaly Detection via Frequency Patching. ICLR 2025.
  • [10] T. Kim, J. Kim, Y. Tae, C. Park, J.-H. Choi, and J. Choo. Reversible Instance Normalization for Accurate Time-Series Forecasting against Distribution Shift. ICLR 2022.
  • [11] J. U. Brandt et al. Reliable Virtual Sensing: A Multi-Domain Benchmark for Robustness Under Sensor Failures. arXiv:2609.18396, 2026.
  • [12] A. Benavoli, G. Corani, and F. Mangili. Should We Really Use Post-Hoc Tests Based on Mean-Ranks? JMLR, 17(5):1–10, 2016.
Questions for authors
  • Can you add Fu & Yan's leave-one-channel-out model [2], PCA reconstruction-based isolation [7, 8], CATCH with RevIN disabled [9, 10], and a detect–isolate–repair arm that substitutes ITX's own reconstruction for flagged channels? If single-pass substitution does not outperform these, what does ITX contribute beyond inference speed?
  • Can you compare DIA and model-side hardening on the same backbone (ModernTCN-PGD/-F2F, or the ITX gate in front of TST-ISensD [11]), report clean RMSE and MuViS-C's worst-case baseline-crossing severity for every system, and measure headroom against the best ungated model, given that the dropout-trained "Naive" is worse than a nominally trained ModernTCN on 7 of 9 datasets (Table 11)? Please also replace Nemenyi with Holm-corrected pairwise Wilcoxon tests on de-duplicated datasets [12].
  • Please report means ± std over at least 3 seeds for Tables 1–3; a factorial ablation crossing corruption type (including VIME-style per-timestep resampling [3]), per-channel embedding, per-channel head, RevIN and K; realized false-alarm rates on clean and corrupted windows with threshold-free AUROC; prevalence-weighted RMSE including multi-sensor faults; and SMD results on all 28 machines with thresholds chosen without test labels. Please also correct Appendix N, which states that ITX is best on localization on 8 of 9 datasets at both lower severities, whereas Table 14 shows 7 of 9 at severity 0.25 (3σ leads on Battery, ALoRa-T on T66-14).
4 comments

We sincerely thank the reviewer for this thorough and constructive review. It pointed us to literature we had missed and prompted important new experiments. Working through these comments has substantially improved the manuscript.

W1 & Q1: Uncited ingredients. Thank you for these pointers. Parts of this lineage are already in the paper: our substitution was inspired by AnomalyBERT (Jeong et al., 2023), the DIA framing follows the fault-diagnosis literature (Isermann, 2006; Blanke et al., 2015), repair is discussed as a defense family (Section 1), and Fu & Yan (2024) in Section 2. However, we missed important precedents and will add them to Sections 2 and 4:

  • VIME and SCARF replace features by draws from their empirical marginals; VIME, like ITX, then reconstructs the original and motivates the corruption the same way. This is even closer to ours than AnomalyBERT. ITX differs in two respects: it swaps a channel's entire window from one other instance, so the substitute is a coherent sensor trace rather than independent per-value draws, and its reconstruction is not a pretext for representation learning but the detector itself, with the residual as the isolation score. The factorial ablation (W3 & Q3) supports the first point: VIME-style resampling is worse on all three datasets.
  • GDN also learns one embedding per sensor and scores per-sensor deviations, but uses the embedding to condition a shared one-step forecaster; ITX unties the input embedding and output head per channel.
  • Self-validating inferential sensors and PCA-based isolation (Qin et al., 1997; Dunia et al., 1996; Alcala & Qin, 2009) are classic precedents for our setting, which we will make explicit in the related work.
  • Sarfraz et al. (2024) show that simple baselines such as PCA reconstruction error rival deep detectors, which supports our 3σ finding; we cite it there.

Close isolators and CATCH without RevIN. We added the three requested isolators, each evaluated in front of the same dropout-trained ModernTCN under the protocol of Tables 1–2:

  • Leave-one-out: ITX's architecture trained with Fu & Yan's objective; at test time, each channel is masked in turn (with zeros, i.e. the channel mean, instead of random in-range values). It needs one pass per channel, so we ran it on the 5 datasets with at most 11 channels.
  • PCA-RBC: reconstruction-based contributions of a static PCA model.
  • CATCH without RevIN: retrained with its tuned configuration.

Detection at 1% FPR and severity 1, and mPC relative to ITX (GM), on the 8 datasets without TEP, whose downstream sweep was not run for the new isolators:

recalllocalizationmPC vs. ITX
ITX.71.781
leave-one-out*.66.78×1.13
PCA-RBC.34.44×1.26
CATCH without RevIN.37.52×1.36
CATCH.29.34×1.50
*5 datasets with at most 11 channels; ITX reaches .72 / .83 there.

ITX outperforms every close isolator downstream on every dataset. Leave-one-out comes closest, but needs one forward pass per channel. On RevIN, the reviewer is right: without it, CATCH detects bias and stuck-at faults, but still remains well behind ITX. We will add this comparison to the appendix and state the RevIN link in Section 5.1.

Repair. We replaced each flagged channel by ITX's reconstruction, as in Fu & Yan (2024), either from the same pass or from a second pass on the healthy channels only, and fed the result to the dropout-trained or the nominally trained predictor. GM over 9 datasets, relative to masking:

mPCclean RMSE
masking (paper)11
one pass → dropout / nominal predictor1.108 / 1.0451.024 / 0.886
second pass → dropout / nominal predictor1.111 / 1.1061.050 / 0.945

Under faults, masking remains best, since the reconstruction partly carries the fault along. On clean data, repair in front of the nominal predictor helps, since false alarms are replaced by a reconstruction instead of zeros, which makes it an option when faults are rare. We will add this comparison to the appendix.

Beyond inference speed. Under faults, ITX outperforms all close isolators and the repair arm, so its advantage goes beyond speed. We are glad the reviewer values the benchmark-scale evaluation and will make it more prominent among our contributions. ITX's contribution lies in combining the ingredients for channel-level isolation, and the factorial ablation (W3 & Q3) shows that this combination matters.

W2 & Q2: We agree that the robustification claim needs controls for the backbone, the metric and the statistics, and we ran the requested comparisons.

Backbone confound. We compared DIA and model-side hardening on the same backbone in both directions: the ITX gate in front of MuViS-C's released TST-ISensD, and our gated ModernTCN against ModernTCN-PGD and ModernTCN-ISensD (full test sets). F2F is defined in MuViS-C as fault-aware pretraining of the TST encoder, so a ModernTCN version would be a new method rather than MuViS-C's. Datasets on which the ITX gate gives the lower mPC:

backboneITX gate vs.ITX gate better
TSTTST-ISensD alone9 / 9
ModernTCNModernTCN-PGD7 / 9
ModernTCNModernTCN-ISensD9 / 9

On TST, the gate closes on average as much of the naive–oracle gap as on ModernTCN, so its benefit is not tied to our backbone.

HR and rPC. Dropping HR leaves ITX's Table 2 GM essentially unchanged (1.007 → 1.008), with the next best model at 1.118, so the lead does not rest on HR. ITX's lead in Table 2 is measured in mPC, which does not depend on clean error; we make mPC the primary metric and report clean RMSE for every system (see also our reply to hmFR, W2 & Q2).

Worst case. We computed MuViS-C's baseline-crossing severity: the lowest severity at which any fault on any channel pushes the RMSE to or above that of the mean predictor. Number of datasets on which a system never crosses (full test sets):

ITX gateTST-F2FxLSTM-Mother 7 MuViS-C models
5 / 94 / 92 / 90 / 9

ITX is also the most robust system in the worst case, and where it crosses, it does so late. On the capped protocol of Table 2, the other gates never cross on at most 2 of 9 datasets, and in our new runs under the same protocol, the ITX gate lifts TST-ISensD from 0 to 6 of 9. We will add the same-backbone comparisons, crossing severities and headroom to the appendix.

Headroom and size of the gains. Against the best ungated ModernTCN per dataset, trained with or without dropout, ITX has lower mPC on 8 of 9 datasets (all but PM10). The reviewer rightly notes that ITX's margin is large on only some datasets. Its advantage is generality: in the full MuViS-C pool, ITX has the lowest mPC on 4 of 9 datasets and is within 5% of the best on all others, whereas every other model is at least 1.8 times worse than the best on some dataset. Since the domain and failure mode are rarely known when a defense is chosen, we consider this generality one of its main practical benefits.

Statistics. As suggested, we replace Nemenyi with pairwise tests of ITX against each of the 9 MuViS-C baselines on mPC: one-sided Wilcoxon signed-rank tests with Holm correction, and the Bayesian signed-rank test with a ±1% region of practical equivalence. PM10 and PM2.5 are two MuViS-C tasks with different targets that share their input channels (App. D). We therefore also test on de-duplicated datasets, counting PM10/PM2.5 once (N=8) or one value per domain (N=6):

N=9N=8, de-duplicatedN=6, one per domain
Holm-Wilcoxon, significant at .057 / 9 baselines5 / 90 / 9
Bayesian signed-rank, min P(ITX better).96.97.95

With all nine datasets, only the two tree ensembles narrowly miss significance (adjusted p = .098). With fewer datasets, the Wilcoxon test quickly runs out of power: with N=8, four baselines narrowly miss (adjusted p = .078), and with N=6, even a win on every domain gives p = 1/64, above .05 after Holm over 9 tests. The Bayesian test has no such floor and gives ITX a probability of at least .95 of being practically better than every baseline. We will report both tests in the final manuscript.

W3 & Q3: Single seed. We retrained all models with seeds 43 and 44 (ALoRa so far on 8 of 9 datasets for detection and 6 of 9 downstream; 3σ is deterministic). mPC (mean ± std) of ITX and the best other gate:

PM10PM2.5Batt.HRTEPVeh.MMRT66-13T66-14
ITX101 ± 167.9 ± .6.022 ± .0024.76 ± .02.05253.24 ± .02.136 ± .004.104 ± .002.109 ± .0001
best other103 ± 169.7 ± .7.0614.71 ± .14.05273.34 ± .02.183 ± .002.124.098 ± .001
CATCHALoRa-Loc3σCATCHALoRa-TALoRa-TALoRa-T3σALoRa-T

The seed variation is small compared with the gaps, and the ranking matches the single-seed tables; only on HR do CATCH and ITX now tie within one std. We will add the results over all seeds to the appendix.

Ablation. We replaced the cumulative ablation by the requested factorial one: every combination of corruption (none, zero-masking, noise, VIME-style, swap) with shared or per-channel embedding and head, plus RevIN and the number of swapped channels, each with 3 seeds on the App. I datasets (PM10, Vehicle, T66-13). mPC relative to ITX for each change, GM over the three datasets:

change to ITXmPC vs. ITX
shared embedding / shared head / both×1.02 / ×1.05 / ×1.12
no corruption / noise / zero-masking / VIME-style instead of swap×1.09 / ×1.05 / ×1.12 / ×1.11
with RevIN×1.43
1 or C/2 instead of C/3 swapped channels×1.02 / ×1.00

Every change to the corruption or the architecture makes ITX worse on average, and ITX has the lowest mPC of all 20 combinations. Untying only one part comes closest and is marginally better on PM10 or Vehicle, but clearly worse on T66-13, where isolation is hardest. The number of swapped channels matters little. We will add the full ablation to the final manuscript.

SMD. We ran all 28 machines with a label-free threshold and retrained ALoRa per machine; the results are in our reply to akjz (W3 & Q2). ALoRa detects slightly better, while ITX localizes better on every metric, most clearly on IPS (27 of 28 machines).

W3 & Q3 (continued): Operating points. All gates are calibrated to 1% FPR on clean validation data. We now report the false-alarm rate realized on clean test windows and, separately, on the healthy channels of corrupted windows, plus the threshold-free AUROC (means over 9 datasets, severity 1):

ITXother gates
false alarms, clean windows1.3%0.6–1.0%
false alarms, healthy channels of corrupted windows3.1%≤ 2.3%
AUROC.91≤ .80

ITX realizes slightly more false alarms, but leads clearly on AUROC, i.e. independently of the threshold. Matching the false-alarm rates does not change the ranking: at a 0.1% target, ITX raises fewer false alarms on clean windows than any other gate at 1% and still has the lowest GM mPC (reply to akjz, W4 & Q4). The Battery case the reviewer points out is real, but these alarms only occur when another channel is faulty, not on clean data, and ITX still has by far the lowest Battery mPC. We will add both false-alarm rates and AUROC to the appendix.

Prevalence and multi-sensor faults. We weighted clean and faulty windows by the share of faulty windows and computed the share above which gating lowers the expected RMSE. We compare against the same dropout-trained predictor without gate (the gate's own cost, as in the reviewer's PM2.5 example) and against the nominally trained, ungated ModernTCN (the full pipeline):

break-even vs.PM10PM2.5Batt.HRTEPVeh.MMRT66-13T66-14
same predictor, ungated24%44%0%4%6%2%5%1%1%
nominal predictor, ungatednever64%2%40%15%1%17%29%18%

The gate itself pays off at a few percent of faulty windows on seven of nine datasets; only on PM10 and PM2.5, where faults barely affect the predictor, does its clean cost dominate, as the reviewer observed. Against the nominal predictor, most of the cost comes from dropout training (reply to hmFR, W2 & Q2), which is therefore the main lever when faults are rare. Beyond the expected error, our focus is reliability: even if faults are rare, a small, constant clean-data cost can be worth paying if the estimate stays usable when a sensor fails (see the worst-case analysis in W2 & Q2). For 2–3 simultaneous faults, see our reply to akjz (W1 & Q1).

Appendix N. Will be corrected (7/9 at severity 0.25). Thank you for spotting this.

Thank you again for this careful review. If anything remains unclear, we are happy to provide further details.

Reviewer_hmFROpenReview ↗
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Paper summary

The paper studies whether identifying and removing faulty input channels improves a virtual sensor’s predictions. It proposes ITX, an iTransformer based detector trained to reconstruct clean windows after selected channels are replaced with traces from other examples. Reconstruction errors identify suspect channels, which are zeroed before a predictor trained with channel dropout. The main evaluation injects faults into one input channel at a time across nine virtual-sensing tasks and ten fault types, comparing practical gates with no-gate and known-fault references. The appendices examine architecture changes, dropout training, clean-input costs, fault severity and test-set size. A separate SMD experiment provides supplementary anomaly-detection and localization evidence.

Critical strengths
  1. Finding faulty channels improves prediction Each gate uses the same fitted dropout-trained predictor, so differences in downstream error are interpretable. ITX reduces corruption RMSE over no gate on all nine tasks. On the full Battery test set, RMSE under corruption falls from .1412 to .0266, while clean RMSE rises from .01108 to .01221. The improvement under faults is substantial, and the clean-performance cost is reported (Tables 2-3, 10-11).

  2. Dropout training helps the predictor handle removed channels Finding and dropping a faulty channel does not ensure that the predictor can work without it. On MMR, adding ITX increases corruption RMSE from .2127 to .3531 without dropout training, but reduces it from .2185 to .1384 with dropout training. Table 11 separates these effects. Lower-severity, failure-mode and full-test checks further support the result within the evaluated setting.

Critical weaknesses
  1. Substitution’s benefit in the final architecture is still unclear. Table 8 shows a benefit from substitution over zero-masking while the channel embeddings and output heads are shared, then adds channel-specific maps under substitution. It does not show whether substitution retains its advantage with the final architecture held fixed. The existing ablation supports the tested combination, but the claim that reconstruction must first detect the faulty channel is stronger than what it establishes (Section 4; Appendix I).

  2. The clean-performance cost of changing both training and gating is unclear. Table 13 already measures the clean cost of adding a gate to the dropout-trained predictor. Table 11 compares predictors trained with and without dropout under corruption, but does not give their matching clean RMSEs. Those values would help assess the cost of adopting both training and gating, especially when faults are infrequent.

Questions for authors
  1. Substitution in the final model. Using the same final architecture with channel-specific embeddings and output heads, is there an existing comparison between substitution and zero-masking? If not, can you distinguish what Table 8 demonstrates from the motivation that reconstruction must first detect the faulty channel?

  2. Clean-performance comparison. What is the clean RMSE of the matched, ungated predictor trained without dropout in Table 11, evaluated on the same windows? Together with the published dropout/gated results, this would complete the comparison for changing both training and gating.

1 comment

We thank the reviewer for the precise review. Both questions ask for comparisons that were indeed missing, and we address them below.

W1 & Q1: You are right that Table 8 adds substitution while embeddings and heads are still shared, so it does not isolate its effect in the final architecture. We have now run that comparison. We trained ITX's final architecture (per-channel embeddings and output heads) once with substitution and once with zero-masking, everything else fixed, with 3 seeds on the App. I datasets (PM10, Vehicle, T66-13); these are fresh runs, so values differ slightly from the single-run Table 8. Mean over seeds (std below 1% for mPC and clean RMSE, at most .015 for precision and recall):

zero / swapPM10VehicleT66-13
mPC110.1 / 108.73.30 / 3.27.116 / .084
clean RMSE106.3 / 106.33.02 / 3.12.0730 / .0727
precision, s = 1.75 / .72.93 / .87.62 / .65
recall, s = 1.52 / .61.99 / .97.39 / .63

With the final architecture held fixed, substitution keeps its advantage under faults, though at a small cost in precision on PM10 and Vehicle. It clearly raises recall on PM10 and T66-13, and on T66-13, where detection is hardest, it also clearly lowers the error under faults. On Vehicle, where both variants detect almost all faults, they perform alike. We will replace Table 8 by the full ablation grid (corruption × shared/per-channel embedding × head) and, in Section 4, present the "must first detect" argument as the design motivation, with this ablation as its empirical support.

W2 & Q2: We agree that adopting the pipeline changes both training and gating, so its clean cost should be measured against the standard predictor. We now report the requested value: the clean RMSE of the ModernTCN trained without dropout and without a gate, on the test windows of Table 13 (row 1). Rows 2 and 3 are Table 13's values:

PM10PM2.5Batt.HRTEPVeh.MMRT66-13T66-14
1. no dropout, no gate (new)90.01260.470.0042.508.0522.831.102.068.074
2. dropout, no gate (Table 13 Naive)94.42262.420.0093.230.0533.019.120.092.090
3. dropout + ITX gate (Table 13)98.90664.451.0093.333.0533.127.126.093.090

The gate itself adds little to the clean RMSE (row 2 → 3). The larger share comes from channel-dropout training, which is essential to the pipeline: as you noted for MMR, gating a predictor trained without dropout can raise the error under faults, and behind the ITX gate the dropout-trained predictor has the lower error on all nine datasets (Table 11). Compared end to end with the standard predictor (row 1), the full pipeline has lower error under faults on 8 of 9 datasets (all but PM10); the fault rates at which this outweighs the clean cost are in our reply to FnVw (W3 & Q3). Reducing the dropout cost is thus the main lever when faults are infrequent, and predictors that are robust to removed channels without losing clean accuracy are a promising direction for future work. We will add this table and this direction to the final manuscript.

Thank you again for this careful review. If anything remains unclear, we are happy to provide further details.

Reviewer_akjzOpenReview ↗
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Paper summary

This paper investigates the vulnerability of data-driven virtual sensors to physical sensor faults (such as drift, bias, and stuck readings). Rather than forcing the virtual sensor to learn invariance over an unbounded fault manifold, the authors propose a Detect–Isolate–Accommodate (DIA) framework: a time-series anomaly detector identifies and masks failing channels at the input, and a downstream predictor (ModernTCN), trained with random channel dropout (ISENSD), predicts from the remaining healthy channels. Observing that standard time-series anomaly detectors often fail to identify which channel is corrupted, the authors introduce ITX—an adapted iTransformer featuring untied per-channel embeddings and projection heads, trained with cross-instance channel substitution. Evaluated on the MuViS-C benchmark across nine datasets and ten failure archetypes, ITX achieves noticeably better channel isolation and downstream virtual sensing robustness than existing baselines.

Critical strengths
  1. Separating fault isolation (front-end) from fault accommodation (channel dropout in the virtual sensor) is well-motivated. It avoids training the primary regression model on complex, multi-parameterized synthetic fault manifolds, reducing accommodation to handling missing inputs.
  2. Table 1 highlights an important blind spot in existing time-series anomaly detection: modern reconstruction models (like CATCH, CrossAD, and ALoRa) often fail to isolate faulty channels under persistent sensor corruptions, frequently trailing a simple per-channel 3σ3\sigma Shewhart baseline.
  3. The modifications in ITX—particularly cross-instance channel substitution—directly target cross-channel dependency modeling. By swapping in real marginal readings from other batch instances, the model cannot rely on trivial out-of-range checks or zero-value artifacts to locate corruptions.
Critical weaknesses
  1. The evaluation strictly tests single-channel corruptions (one victim sensor at a time). In industrial systems, multi-sensor degradations or shared power/bus issues often cause concurrent failures. Moreover, the DIA pipeline fundamentally relies on the sensor array having enough functional redundancy to estimate the target after dropping a channel. The paper does not analyze how performance degrades when critical, non-redundant channels fail.
  2. When a channel is flagged, Equation (2) zeroes out that entire channel across all TT time steps of the window. For transient corruptions (such as sporadic outliers), discarding hundreds of time steps of healthy data just because of a brief spike seems inefficient. This likely explains why CATCH outperforms ITX on noise and outliers in Table 12.
  3. In Section 5.3, the generalization of ITX to standard anomaly detection is evaluated solely on a single machine (machine-1-1) from the Server Machine Dataset (SMD). Evaluating only one entity out of 28 makes it hard to conclude whether ITX generalizes across standard TSAD tasks, especially since the detection threshold in Table 4 was tuned directly on the test labels.
  4. In Table 13, ITX ranks last among all gates in clean-data RMSE (geometric mean 1.025 vs. 1.002 for naive). Because ITX maintains higher recall under fault conditions, its slightly higher false-positive rate leads to unnecessary masking on clean data, introducing a measurable penalty during normal operation.
Questions for authors
  1. ITX is trained with k∼Unif{1,…,⌊C/3⌋}k \sim \text{Unif}\{1, \dots, \lfloor C/3 \rfloor\} swapped channels per window. How does the full DIA pipeline perform when two or three correlated sensors fail at the same time during testing? Does the attention mechanism continue to isolate all faulty channels, or do multiple corruptions cause masking errors?
  2. Why was Section 5.3 restricted to machine-1-1 of SMD? Does ITX maintain its F1 and IPS gains when evaluated across the entire SMD benchmark, or on other standard multivariate datasets like PSM or SWaT?
  3. For short-duration faults like outliers or intermittent noise, did the authors consider localized interpolation or timestep-level masking instead of zeroing the whole context window? Would preserving the uncorrupted segments of the window help close the remaining gap to the oracle?
  4. Thresholds τc\tau_c are calibrated at a fixed 1% validation FPR. How does downstream virtual sensing performance change if the FPR target is tightened to 0.1% (to protect clean-data accuracy) or loosened to 5% (to catch weaker incipient drifts)?
2 comments

We thank the reviewer for the encouraging feedback and the helpful questions, which we address below.

W1 & Q1: We focused on single-sensor failure first, which lets us cleanly disaggregate the impact of each failure mode. We agree that multi-sensor degradation is an important setting, and we have run the experiments you suggested.

We let 2–3 channels fail simultaneously, on 10 random sets and up to 10 of the most correlated sets per dataset (|Pearson| on clean training data). All failing channels share the failure mode and severity, as with a common cause such as a bus fault. We use all 9 datasets, the test windows of Tables 1–3, all 10 failure modes at severities 0.25, 0.5 and 1, and the unchanged gates and thresholds; the oracle zeroes all failing channels. The table reports rPC as in Table 3 (over these three severities) and ITX's detection at severity 1 as in Table 1:

victimsungated3σITXoracleITX recall per victimITX false alarms on healthy channels
1 (paper, same severities)2.211.611.231.04.723.1%
2, random2.942.001.491.09.725.5%
2, correlated3.432.291.671.10.736.5%
3, random3.152.201.691.17.698.6%
3, correlated4.022.702.101.35.709.1%

With 2–3 concurrent failures, the ITX gate still closes most of the gap to the oracle; correlated failures are the hardest case. Recall per failing channel is unchanged, so one fault does not mask another, while false alarms on the remaining healthy channels rise with the number of failures (up to 9.1%).

Non-redundant channels: since the paper's runs corrupt every channel in turn, we can measure how much the oracle loses when a channel is dropped. Only 9 channels in 4 datasets cost it more than 10%, and ITX detects faults on these at least as reliably as on the other channels (e.g. recall .78 vs. .54 on MMR). The remaining loss thus comes from the missing information, not from isolation.

We will add these results to the final manuscript and plan to further investigate multi-sensor failures and redundancy in future work.

W2 & Q3: We did consider this and deliberately chose a conservative rule: once a sensor misbehaves, it is not trusted for the whole window. We agree, however, that for sporadic faults such as outliers, finer-grained masking could preserve useful data, provided both the gate and the virtual sensor are trained for it; Section 6 already names this as an extension. We have now tested it.

We retrained both components for partial faults: ITX with partial-window swaps (a random segment or scattered timesteps of a swapped channel) and the ModernTCN with additional partial dropout. Within a flagged channel, we then either zero only the timesteps whose residual exceeds a per-channel threshold at the same 1% FPR (timestep masking), or replace them by ITX's reconstruction (localized interpolation), and compare both with masking the whole window. Change in mPC relative to the paper's configuration on the App. I datasets (PM10, Vehicle, T66-13; GM, negative is better):

failure modewhole windowtimestep maskinglocalized interpolation
outliers−1.4%−3.7%−3.6%
noise−0.8%−2.2%0.0%
bias+5.2%+6.9%+23.1%
hard fault+6.0%+8.5%+22.3%
linear drift+3.1%+4.8%+10.7%
nonlinear drift+3.2%+5.4%+8.9%
scaling+1.5%+0.9%+0.2%
time-varying scaling+0.7%−1.0%−3.2%
trimming, constant−0.9%−1.5%−1.5%
trimming, varying−1.1%−1.1%−1.0%
all modes (mPC)+1.7%+1.9%+6.2%

W2 & Q3 continued: As you expected, keeping the healthy timesteps helps on sporadic faults: timestep masking is best on outliers and noise. On persistent faults, whole-window masking remains best, and interpolation is clearly worse, since ITX's reconstruction absorbs part of the fault. Overall, timestep and whole-window masking are on par, so choosing the granularity per fault is a promising extension. We will add this ablation to the final paper.

W3 & Q2: We followed ALoRa's protocol (Shimillas et al., 2026), whose released SMD setup uses only machine-1-1 and selects the threshold on the test labels. We have now run all 28 machines, one model per machine without tuning, and add a label-free threshold (99th percentile of training scores, i.e. 1% FPR as in our main protocol).

F1, threshold from test labelsF1, label-freeHR@100/150NDCG@100/150IPS@100/150
ITX, machine-1-1 (Table 4).97–.51 / .64.51 / .58.80 / .89
ALoRa, machine-1-1 (published).97–.56 / .76.60 / .70.60 / .81
ITX, all 28 machines.89.76.53 / .67.56 / .63.75 / .88
ALoRa, all 28 machines (retrained, authors' code).91.81.42 / .56.43 / .51.44 / .60

Across all machines, ALoRa detects slightly better, while ITX localizes better on every metric, most clearly on IPS (27 of 28 machines). We will add the results on all 28 machines and the label-free threshold to Section 5.3 of the final manuscript. If you consider a further benchmark important, we are happy to add SWaT, which provides channel-level labels, to the final version.

W4 & Q4: We fixed the target at 1% FPR so that all detectors are compared at the same operating point, but agree that it governs the trade-off between clean accuracy and robustness. As suggested, we varied it.

We recalibrate ITX's thresholds to 0.1% and 5% FPR on clean validation data and rerun the protocol of Tables 2, 3 and 13 (all 9 datasets, same corrupted inputs, same dropout-trained ModernTCN). The table gives the GMs of Tables 13, 2 and 3:

systemfalse alarms on clean windowsrecall (s=1)clean RMSEmPCrPC
Naive (ungated)––1.0021.6892.081
ITX, target 0.1%0.3%.621.0051.0211.265
ITX, target 1% (paper)1.3%.721.0251.0111.218
ITX, target 5%4.6%.821.0611.0681.258
Oracle (reference)––1.0020.8461.041

At 0.1%, the clean-data cost nearly vanishes (1.005 vs. 1.002 for Naive), while mPC rises only slightly and stays well below that of every other gate in Table 2 at 1% (≥ 1.306). At 5%, ITX catches more weak drifts but is worse on both, since the extra false alarms remove useful channels. The clean-data penalty in Table 13 is thus a matter of the operating point. Thank you for this suggestion: 0.1% removes nearly all of the clean-data cost at only a small loss under faults, and we will report it alongside 1% in the final manuscript.

Thank you again for these constructive suggestions. If anything remains unclear, we are happy to provide further details.

Comments on the paper

1 comment

We thank all reviewers for their constructive and detailed feedback. As the discussion period ends today, we would be grateful if the reviewers could let us know whether our responses address their concerns. We are happy to clarify anything further. Among other points, we addressed the main comments by:

(1) Adding stronger baselines and controls (FnVw). We added closely related isolation methods (leave-one-channel-out, PCA-RBC, CATCH without RevIN) and a repair arm. ITX outperforms each isolator downstream on every dataset, and masking beats repair on average. On the same backbone, the ITX gate also beats model-side hardening (ModernTCN-ISensD: 9/9 datasets, ModernTCN-PGD: 7/9), and it is the most robust system in the worst case.

(2) Strengthening the evidence for ITX's design (hmFR, FnVw). We report 3 seeds and a factorial ablation of 20 configurations, which shows that substitution keeps its advantage under faults in the final architecture.

(3) Testing beyond the original setup (akjz, FnVw). We ran 2–3 simultaneous (incl. correlated) failures and timestep-level masking for sporadic faults. We also ran SMD on all 28 machines with label-free thresholds, where ITX localizes better on every metric while ALoRa detects slightly better.

(4) Quantifying the clean-data cost (akjz, hmFR, FnVw). We separate the cost of the gate from the cost of dropout training, give break-even fault rates, and show that a 0.1% FPR target nearly removes the gate's own cost.

(5) Revising statistics and related work (FnVw). We add Holm-corrected Wilcoxon and Bayesian tests on de-duplicated datasets, and the missing references (VIME, SCARF, GDN, self-validating and PCA-based sensor validation).

Further results and clarifications are in the individual responses.

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