acceptodds
Under review as a conference paper at ICLR 2027

Augmenting Visual Anomaly Detection with Automated Interpretability

Abstract

Visual anomaly detectors identify deviations from known-normal data, but their anomaly signals may mix evidence of actual anomalies with benign visual variation. We investigate whether automated interpretability can augment visual anomaly detectors by identifying and intervening on different components of this signal. We decompose PatchCore nearest-normal residuals into sparse features using Sparse Autoencoders (SAEs), and provide high-activation and contrastive non-active examples to a Multimodal LLM, which describes each feature and labels it as anomaly, distractor, or uncertain. These labels guide interventions in the SAE hidden representation, where distractor features are suppressed and anomaly features amplified. The edited representation is then used to reconstruct patch embeddings, which are rescored with PatchCore. Across 40 categories from four benchmarks, applying both interventions jointly improves macro-average image-level AUROC from 0.8724 to 0.8857 on source data and from 0.8066 to 0.8210 under synthetic corruptions. On three additional RobustAD categories with real acquisition shifts, the same interventions improve AUROC from 0.8745 to 0.9056 on source data and from 0.6069 to 0.6599 under real acquisition shifts. Finally, individual feature interventions across all 43 categories show that the MLLM labels are aligned in aggregate with how features differently affect normal and anomalous images. Our code is available at https://anonymous.4open.science/r/vad-interp-EFE8.

Primary area:
interpretability and explainable AI
Keywords:
mechanistic interpretability, anomaly detection, robustness

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_y8JXOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This work applies sparse autoencoders (SAE) and multimodal large‑language‑model(MLLM) automated interpretability to improve frozen visual anomaly detectors (primarily PatchCore). The pipeline decomposes anomaly residuals from patch embeddings into sparse SAE features; an MLLM labels each feature as anomaly / distractor / uncertain using high‑activation and contrastive examples. It suppresses distractor features and amplifies anomaly features, then reconstructs patch embeddings for rescoring. Evaluations cover 43 categories across five benchmarks, including synthetic corruptions and real‑world acquisition shifts from RobustAD. Joint intervention lifts macro AUROC from 0.8724 to 0.8857 on source data, and brings larger gains under real distribution shifts. Ablations study SAE hyper‑parameters, MLLM alternatives, other anomaly detectors and vision backbones.

Critical strengths

This work propose a new paradigm, which uses automated mechanistic interpretability to boost downstream anomaly‑detector performance, whereas most prior SAE‑MLLM interpretability work focuses only on understanding model behaviour. This paper turns interpretability into actionable intervention: semantic labels from MLLM directly modify internal representations to improve detection. It establishes a practical use‑case for mechanistic interpretability beyond pure explanation research.

Critical weaknesses
  1. The proposed method requires calibration set containing anomalous samples, breaking the “normal‑only” premise of unsupervised anomaly detection. As we known, standard industrial anomaly detection only uses normal images for training, but this method needs a balanced calibration set with both normal and anomalous examples to train SAE and select amplification α. Even though the base detector remains normal‑only, the intervention pipeline depends on anomaly examples, limiting real‑world zero‑shot / purely‑normal‑only deployment.
  2. Ablations show performance gains are not universally transferable. For the FRE detector and WideResNet‑50‑2 backbone, interventions deliver negligible or zero improvements. MLLM feature label agreement between different open‑source LLMs is moderate (~67‑81%). While gains persist on average, there is no guarantee of improvement for arbitrary backbones / detectors, which limits general applicability.
Questions for authors
  1. How sensitive is the SAE feature quality and subsequent MLLM labeling to the diversity and count of anomalous samples in the calibration set? Specifically, how does performance behave if test anomalies differ fundamentally in type from those present in calibration?
  2. Could you quantify the end-to-end inference latency added per image by the nearest-neighbor residual computation, SAE encoding/decoding, and secondary memory-bank rematching compared to standard PatchCore?
1 comment

Thank you for taking the time to review our paper.

W1. We already explicitly acknowledge this limitation in the paper. However, calibration sets containing some anomalous examples are not extraneous to normal-only anomaly detection, as even detectors trained exclusively on normal images may use anomalous examples to select a decision threshold or calibrate anomaly heatmaps. We agree that our approach would not apply in scenarios where no anomalous examples are available. Such scenarios certainly exist, for example when introducing a new product, but we are less convinced that they are representative of industrial anomaly detection as a whole.

W2. We never claimed that our interventions guarantee improvements, and we already explicitly acknowledge this in the limitations paragraph. SAE training and MLLM labels introduce variability, and this is largely an empirical paper. What we show is that interventions improve performance on average across many categories, particularly under synthetic corruptions and even more under real acquisition shifts. Regarding detectors, with FRE we see strong improvements on source images, while results are mixed under synthetic corruptions. Regarding backbones, we see improvements with SwinV2, but not with WideResNet-50-2. We ran several ablations, and using all 43 categories for all of them was not feasible, especially those involving MLLM labeling. Both the detector and backbone ablations therefore cover 5 categories, and further investigation could help us better understand the cases where improvements do not seem to transfer. Regarding the MLLMs, we would not consider 81.1% agreement between GPT and Gemma across 640 feature labels particularly low. Qwen agrees less with the other two models (67.8–69.5%), and its results are slightly lower. Still, all three improve over original PatchCore with joint intervention on both source and corrupted data.

Q1. We added experiments in Appendix H investigating calibration size and sensitivity to the selection of calibration examples, retraining the SAE and regenerating the MLLM labels for each configuration. Increasing calibration size generally improves SAE reconstruction quality, with diminishing returns in downstream performance. Across five calibration splits, AutoInterp consistently outperforms calibration-guided interventions, with relatively limited performance variability. Regarding unseen anomaly types, we added Appendix I, where we evaluate 20 categories with defect types entirely absent from calibration. We found that AutoInterp joint improves over original PatchCore on both seen and unseen defects, under source and corrupted conditions. Interestingly, calibration-guided joint performs better on seen defects, while AutoInterp performs better on unseen defects, where calibration-guided joint even falls below original PatchCore.

Q2. We added Appendix J with an inference latency benchmark across all 43 categories. On an NVIDIA L40S with batch size 1, original PatchCore takes 51.06 ± 6.13 ms per image, while AutoInterp joint takes 75.94 ± 11.34 ms, corresponding to an additional 24.88 ± 5.33 ms per image (48.7% overhead). Most of the overhead comes from SAE processing and secondary nearest-neighbor rematching.

We believe we have addressed all of your points, but if anything remains unclear or unconvincing, we would be happy to clarify. Thank you again for the constructive review.

Reviewer_MQ7QOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The submission proposes to decompose nearest-normal residuals into sparse representations with a tiny per-category SAE, which is trained on a set that incorporates anomalies. An LLM labels each representation as anomaly, distractor or uncertain. Distractors are zeroed and anomaly features are strengthened, and the edited embeddings are rescored. When evaluated on 40 classes from 4 benchmarks improvements are observed while ablations test the LLM, SAE settings and amplification factor. The detector and backbone ablations focus on only five classes and yield mixed results.

Critical strengths
  • strong controls support the claim that semantic labels provide additional information
  • feature-level causal test yields interpretability above end-metric gains
  • good ablations
Critical weaknesses
  • small gains
  • requirement for labeled anomalies
  • interpretability is only partly validated
Questions for authors

what are confidence intervals for the three RobustAD classes?

1 comment

Thank you for taking the time to review our paper.

W1. We acknowledge that some improvements are modest, particularly on source data. However, this should be considered in the context of visual anomaly detection, where performance is often already close to saturation. For example, PatchCore itself, which is considered a landmark method in visual anomaly detection, improved image-level AUROC on MVTec AD from 97.9% to 99.1% over the strongest previous baseline, a gain of only 1.2 percentage points. In our case, we further improve an already strong PatchCore detector, with substantially larger gains under distribution shifts, reaching +5.30 AUROC points on RobustAD under real acquisition shifts. Moreover, even small absolute gains near saturation can be meaningful. For instance, improving AUROC from 0.98 to 0.99 means halving the proportion of normal–anomalous image pairs that the detector ranks incorrectly.

W2. We already explicitly acknowledge this limitation in the paper. However, calibration sets containing some anomalous examples are not extraneous to normal-only anomaly detection, as even detectors trained exclusively on normal images may use anomalous examples to select a decision threshold or calibrate anomaly heatmaps. Our approach would not apply in scenarios where no anomalous examples are available. Such scenarios certainly exist, for example when introducing a new product, but we are less convinced that they are representative of industrial anomaly detection as a whole.

W3. We acknowledge that in RQ3 we evaluated the feature labels (anomaly, distractor, uncertain), but not their descriptions. This was mainly because our method uses the labels to guide interventions, while the descriptions are not directly used. Nevertheless, we acknowledge that evaluating the descriptions would provide additional evidence of their reliability. We therefore added Appendix D, where, following an evaluation inspired by Paulo et al. (ICML 2025), we test whether an independent MLLM can distinguish activating from non-activating image regions based on the generated descriptions. We found that the descriptions consistently outperform shuffled controls, with discrimination accuracy increasing with feature activation strength. This supports that the descriptions contain information about feature activations, while we maintain, as already acknowledged in the limitations paragraph, that SAE features may be polysemantic and that their descriptions are not guaranteed to be faithful.

Q1. We computed 95% confidence intervals for the AUROC improvement of AutoInterp joint over original PatchCore using 10,000 paired, class-stratified bootstrap resamples. Across RobustAD, the average improvement is +3.11 [1.45, 4.89] AUROC points on source data and +5.30 [3.63, 6.95] under acquisition shifts. For the individual categories, the improvements are +5.39 [1.66, 9.52] on source and +12.65 [8.19, 17.12] under shifts for PCB, +3.24 [−0.05, 6.58] and +1.60 [−0.33, 3.42] for MetalParts, and +0.71 [0.03, 1.89] and +1.67 [0.31, 3.07] for PiledBags, respectively.

We believe we have addressed all of your points, but if anything remains unclear or unconvincing, we would be happy to clarify. Thank you again for the constructive review.

Reviewer_63GPOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper investigates whether automated interpretation of sparse features can improve a frozen visual anomaly detector. It trains a TopK sparse autoencoder on PatchCore residuals from normal and anomalous calibration images. A multimodal LLM interprets activating and non-activating examples and labels each feature as anomaly, distractor, or uncertain. These labels guide amplification or suppression before reconstructing and rescoring patch embeddings, while preserving the SAE reconstruction error. The evaluation covers 40 categories across four benchmarks, synthetic corruptions, and three RobustAD categories with real acquisition shifts.

Critical strengths
  1. The paper proposes an interesting way to use automated interpretability to improve anomaly detection. The authors use the MLLM’s interpretations of SAE features to suppress distractor features and amplify anomaly features, rather than using these interpretations only to explain predictions. This provides a useful connection between feature interpretation and detector performance.
  2. The authors evaluate the method across 40 categories and consider both synthetic corruptions and real acquisition shifts. They also include calibration-guided and random interventions, along with several ablations, to understand the contribution of different components. In particular, the evaluation on real acquisition shifts provides useful evidence of the method’s effectiveness beyond synthetic corruptions.
Critical weaknesses
  1. Calibration set construction and reliability: In Section 4, the authors construct balanced calibration sets by selecting 20% of the smaller test class for each class. These sets contain 4–54 images, while RobustAD uses larger sets with a median of 150 images. However, there is no clear justification for choosing a balanced ratio or the 20% budget, and it is unclear how performance changes with different calibration sizes and class ratios. The correlations reported in Section 5 do not directly address this concern because they compare different categories, where difficulty and other factors also vary. Tables 1–2 also do not report uncertainty estimates or results across repeated calibration splits for the proposed method. This is important because, on the 40-category benchmark, the improvement over calibration-guided joint intervention is only 0.46 AUROC percentage points on source data and 0.20 points under corruption. The authors themselves acknowledge in Appendix C that selecting the amplification factor on a small calibration set may overfit category-specific variation. Also, the calibration budget depends on labeled class counts from the original test set, which would generally not be available beforehand in deployment. The authors should evaluate fixed calibration budgets, different class ratios, and repeated calibration splits to better establish the reliability of the reported improvements.
  2. Feature interpretation and disentanglement: The authors assign each SAE feature a single MLLM label and apply the corresponding intervention wherever that feature activates. However, it is unclear whether individual features consistently separate anomaly-related information from benign variations or capture multiple concepts. Although the qualitative examples and RQ3 analysis provide some support, they do not directly establish feature purity. Also, significant normal–anomalous differences for anomaly features and nonsignificant differences for distractor features do not by themselves establish that the two groups behave differently.
  3. Limited comparison with existing methods: The authors include useful controls, such as a linear probe and calibration-guided interventions. However, they do not compare against established anomaly detection methods that also use a small number of anomalous examples. The FRE experiment in Appendix E mainly tests whether the framework extends to another detector. Given the small improvement over calibration-guided intervention in Table 1, comparisons with representative methods using the same calibration data and evaluation splits would better establish the additional benefit and practical competitiveness of the approach.
  4. Generalization to unseen defect types: The authors separate calibration and evaluation images but do not specify whether any defect types are excluded entirely from calibration. It is therefore unclear whether the improvements extend to unseen defects or mainly benefit defects represented in the calibration set. Preserving reconstruction error does not necessarily protect unseen-defect information captured by features labeled as distractors. The authors should evaluate defect types excluded from calibration and compare performance with the original PatchCore.
Questions for authors
  1. Calibration protocol and stability: What motivated the balanced 20% sampling policy? Are the improvements over calibration-guided intervention consistent across repeated calibration splits, with uncertainty estimates?
  2. Matched comparisons: Are comparisons available with established anomaly detection methods using the same anomalous calibration examples and evaluation splits?
  3. Unseen defects: Do the evaluation sets include defect types entirely absent from calibration? If so, how does performance compare with original PatchCore on represented and unseen defects separately?
3 comments

Thank you for taking the time to review our paper.

W1–Q1. We added Appendix H with four new experiments to investigate the sensitivity of the method to the calibration protocol, evaluating different calibration sizes, class ratios, repeated calibration splits, and fixed calibration budgets. We found that AutoInterp improves over the original detector across all tested calibration sizes and fixed budgets, with diminishing returns as the budget increases. Its advantage over calibration-guided interventions also persists across all five calibration splits. With imbalanced calibration, AutoInterp generally outperforms the baselines, although performance is often lower than with balanced calibration, and class weighting partially mitigates this effect. We also added confidence intervals for the main results and the repeated split comparisons.

W2. We never claimed that SAE features are pure or completely monosemantic, and we are not aware of any interpretability method that can guarantee this. We acknowledge, however, that in RQ3 we evaluated the feature labels (anomaly, distractor, uncertain), but not their descriptions. This was mainly because our method uses the labels to guide interventions, while the descriptions are not directly used. Nevertheless, we agree that evaluating the descriptions would provide additional evidence of their reliability. We therefore added Appendix D, where, following an evaluation inspired by Paulo et al. (ICML 2025), we test whether an independent MLLM can distinguish activating from non-activating image regions based on the generated descriptions. We found that the descriptions consistently outperform shuffled controls, with discrimination accuracy increasing with feature activation strength. This supports that the descriptions contain information about feature activations, while we maintain, as already acknowledged in the limitations paragraph, that SAE features may be polysemantic and that their descriptions are not guaranteed to be faithful. We also extended RQ3 with direct statistical comparisons between anomaly and distractor features, finding significant differences under both suppression and amplification.

W3–Q2. We are not proposing a new anomaly detection method, but investigating whether automated interpretability can augment existing ones. This is why, for both PatchCore and FRE, we compare the original detector against its augmented version. Regarding methods using anomalous examples, we identified DRA (CVPR 2022), whose reported performance is already below original PatchCore, and IDEAL, which was very recently accepted at NeurIPS 2026, and whose full implementation was released after our submission deadline. Furthermore, IDEAL addresses a completely different problem, as it trains on one anomaly detection dataset and performs few-shot detection on another, using only a few examples from the target categories. We therefore do not think that comparing against IDEAL would be meaningful. If you have a specific method in mind that we may have overlooked and consider an important missing baseline, we can investigate whether a comparison is feasible.

W4–Q3. We added Appendix I, where we evaluate 20 categories, separating defect types represented in calibration from those entirely absent, using the same normal test images for both groups. We found that AutoInterp joint improves over original PatchCore on both seen and unseen defects, under source and corrupted conditions. Interestingly, calibration-guided joint performs better on seen defects, while AutoInterp performs better on unseen defects, where calibration-guided joint even falls below original PatchCore.

We believe we have addressed all of your points, but if anything remains unclear or unconvincing, we would be happy to clarify. Thank you again for the constructive review.

The additional experiments partly address W1. However, the calibration-size, class-balance, and repeated-split experiments cover only two categories, and the fixed-budget experiment covers five. This leaves open whether the findings extend across the benchmark, especially when anomalous calibration examples are scarce. Table 16 shows sensitivity to calibration composition, including the number of anomalous examples. FRE is evaluated separately but is missing from the calibration experiments. Including it would help establish whether the findings extend beyond PatchCore. I would also like to see comparisons with recent methods that use a similar number of anomalous examples. For W2, the direct statistical comparisons resolve the statistical part of my concern. My concern about individual features remains: each SAE feature receives a single MLLM label, and the corresponding intervention is applied wherever that feature activates. What happens if the same feature captures anomaly information in some cases and benign variation in others? Appendix D shows that the descriptions help identify activating regions, but it does not directly test this possibility. Appendix I resolves my W4 concern by reporting separate results for seen and unseen defect types across 20 categories. I appreciate the authors’ additional work. The remaining questions about feature-label consistency and the limited coverage of the calibration experiments are substantial enough that I am keeping my rating unchanged.

W1 (Follow-up): Calibration-ablation coverage

We conducted several ablation studies and had to use subsets of categories because running all of them on the full 43 categories would have been computationally infeasible. Considering only the calibration ablations added during rebuttal, these include calibration-size sensitivity (2 new runs × 2 categories), class-balance sensitivity (4 new runs × 2 categories), repeated splits (4 new runs × 2 categories), and fixed calibration budgets (2 new runs × 5 categories). Each run requires SAE training, MLLM feature labeling (roughly $3 in API costs per run), and downstream intervention evaluation on source and corrupted images. Similarly, when ablating components such as the anomaly detector, MLLM, SAE configuration, or vision backbone, we conducted the ablations separately. If we instead started mixing these with the other ablations, the number of combinations would have exploded.

The experiments addressing the main contributions and research questions of our paper already cover all 43 categories, while these supplementary ablations investigate sensitivity to specific calibration choices. We hope this clarifies why we had to reduce the coverage of these supplementary ablations. If you still believe additional categories are necessary, we would appreciate more clarity on which specific calibration ablations require more categories and how many would be sufficient. We would be open to extending those ablations within reason.

W2 (Follow-up): What happens if a feature activates in both anomalous and benign patches?

We added a new Appendix K that investigates this, covering all 43 categories. Specifically, we investigate how often distractor features activate at the decisive patch of anomalous images and anomaly features at the decisive patch of normal images, and how often the corresponding interventions worsen the individual image's ranking contribution to AUROC. We find that activation and worsening of the individual image's ranking contribution occur together in 1.38% of feature–image pairs for distractor features and 9.04% for anomaly features.

As already acknowledged in our limitations, individual SAE features may be polysemantic, and we never claimed that interventions improve the ranking of every single image.

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

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