acceptodds
Under review as a conference paper at ICLR 2027

Reconstruction-Based Anomaly Detection in Positive-Unlabeled Reverse Distillation

Abstract

Reverse distillation is one of the strongest paradigms for visual anomaly detection, training a student decoder to reconstruct a frozen teacher encoder's representations so that unseen anomalies yield disproportionately large reconstruction errors. However, this paradigm implicitly assumes a training pool of only normal samples. In practice, such pool is often contaminated, modeled as a mixture of normal and anomalous distributions at an unknown rate, and training directly on this mixture provides no pressure to separate the two populations. Positive-unlabeled learning (PUL) offers a natural way to address this, incorporating a small labeled anomalous set to guide this separation. However, existing PUL approaches largely rely on classification-level objectives that offer little sense of where an anomaly is located. Instead, we build directly on the spatial structure of reconstruction error in feature space, which already carries information about where an anomaly might be located, without requiring pixel-level annotation. We propose an objective that thresholds each image's own feature-space reconstruction error into anomalous and normal regions and applies separation pressure between them. We apply this pressure asymmetrically. For labeled anomalies, whose status is certain, we push the two regions apart in both directions. For unlabeled samples, we only push the flagged region's error down. Evaluated on Real-IAD, an industrial anomaly benchmark, our method consistently improves over the uncorrected baseline and recovers much of the performance gap to an oracle trained without contamination.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Anomaly Detection, Positive-Unlabeled Learning, Reverse Distillation

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_3MAMOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes a spatial positive–unlabeled training objective for reconstruction-based anomaly detection with contaminated training data and a small set of labeled anomalies. Building on a DINOv2 reverse-distillation backbone, it uses per-image Otsu thresholding to divide reconstruction-error maps into flagged and complementary regions. An asymmetric objective combines reconstruction on unlabeled images with a positive-sample hinge loss and a complementary-region anchor. Results across 30 Real-IAD categories show encouraging detection and localization improvements, although the theoretical interpretation and experimental attribution require further clarification.

Critical strengths
  1. Practical problem, and the spatial objective makes sense. The paper tackles contamination in supposedly normal training data while only using image-level anomaly labels. I like the way it treats labeled anomalies and uncertain unlabeled samples differently: confirmed anomalies get separation pressure, while unlabeled ones only get reconstruction pressure. This seems like a useful design principle for bringing limited anomaly supervision into reconstruction-based detectors.
  2. The reported gains are quite encouraging across a fairly diverse benchmark. On 30 Real-IAD categories, Table 1 shows mean Image-AUROC going from 0.869 to 0.928 and PRO from 0.932 to 0.956 over RD. The evaluation covers both detection and localization, and Appendix B gives significance tests across categories instead of relying only on aggregate numbers.
Critical weaknesses
  1. The evaluation is limited to Real-IAD. Real-world industrial defects vary widely in appearance, size, and type. Although Real-IAD covers 30 categories, results on a single dataset provide limited evidence of generalization. Additional experiments on datasets such as MVTec AD and VisA under the same PU setting would strengthen the evaluation.
  2. The computational efficiency is not evaluated. The paper provides training settings but does not report training time, inference speed, or GPU memory usage. A comparison with RD and other baselines would help clarify the extra cost of the proposed training objective and its practicality for industrial applications.
  3. The benefit of Otsu thresholding is not directly verified. The paper argues that per-image adaptive thresholding is preferable to fixed top-kk selection, but does not compare them under the same training objective. Such a comparison would help establish whether the adaptive split contributes to the reported gains.
  4. The impact of contamination rate is not sufficiently explored. Handling contaminated training data is central to this work, but the paper does not systematically evaluate how performance changes as the contamination rate increases. Such experiments would help clarify the method’s robustness under different levels of contamination.
Questions for authors

Please see weaknesses.

2 comments

We thank the reviewer for the useful comments. In the following, we address the questions and the weaknesses.

Evaluation beyond Real-IAD (added to the Supplementary Material, Section "Additional quantitative results"). We added results on VisA and MVTec AD under the same PU setting (Tables 6 and 7), where our method also outperforms or is comparable to the selected baselines.

Computational cost (added to the Supplementary Material, Section "Computational cost"). We report training time, inference cost and GPU memory for all methods, measured on a single H200 GPU (VisA; 50 epochs and batch 16 for gradient-trained methods). Inference: our method uses the Dinomaly architecture, so its inference cost is identical to RD (229.6 GFLOPs, 29 ms/image). Training: the only extra cost is passing one labeled mini-batch P\mathcal{P} through the student alongside U\mathcal{U} (the Otsu split is negligible), which gives ≈1.3×\approx1.3\times RD's training time (17.2 vs. 13.4 min on cashew, 30.0 vs. 22.8 min on candle) and 19.3 vs. 13.4 GB peak memory. LOE, SOEL and PUAE are adapted to the same architecture, so they share its inference cost. SOEL and PUAE also use P\mathcal{P} in their loss and match our training cost, while LOE matches RD. MeDS is about 8$\times$ more expensive to train (135 min over three stages). SoftPatch builds its memory bank quickly but is about 5$\times$ slower at inference (148 ms/image) due to nearest-neighbour search. In industrial use, a model is trained once and then inspects every product on the line, so a one-time training overhead with unchanged inference cost is practical.

Otsu split vs. fixed top-kk (added to the Supplementary Material, Section "Additional ablations"). We constructed an ablation Otsu split vs. a fixed top-kk selection, e.g., for k=5%k=5\%. We trained this ablation under the same objective on VisA dataset. Image-AUROC is comparable between the two, but PRO (localization) consistently favors the Otsu split. We attribute this to defect size varying across images.

Additionally, we performed the following diagnostics. We visualize the dynamics of the inside/outside separation on the hidden GT defect mask over training on the unlabeled dataset Utrain\mathcal{U}_{\text{train}} (Fig. 7). Early in training, the fixed top-5%5\% split's separation is briefly higher than Otsu's (the model is still training and not yet converged). It then degrades monotonically for the rest of training, ending lower than Otsu's. Real defects occupy a different, and unknown in advance, fraction of the image than the fixed size. Therefore, the fixed split can end up pushing down (anchoring) genuine defect pixels, or pushing up (hinging) genuine background pixels, instead of the correct ones. In contrast, Otsu's separation does not degrade as much as the top-5%5\%.

Impact of the contamination rate (added to the main text, Section "Ablation study"). We sweep the contamination rate α\alpha of the unlabeled pool while keeping the labeled pool and the test split fixed, on both Real-IAD and VisA (Fig. 4). The gap between our method and RD grows monotonically with the contamination rate, for both Image-AUROC and PRO. Please see our response to Reviewer z6cF (point "Sensitivity analysis", a) for the full setting and discussion.

Reviewer_3MAMOpenReview ↗

My opions after reading the rebuttal

Thanks for the detailed response. The newly added experiments on MVTecAD and ViSA strengthen the paper greatly. Yet, the evaluation metrics adopted are limited (I-AUC and PRO), it is recommended to incorporate more comprehensive metrics, such mAD [1] to see its effectiveness comprehensively. Minor issues: Inconsistent symbols for metrics, such as AUC-I and I-AUC. Besides, this method depends on Dinomaly. However, the reviewer thinks it should not be treated as a baseline, as it is trained without any correction. It should design an experiment by adding some naive baseline upon Dinomaly tailored to this setting. Moreover, Dinomaly, which is misdescribed as "RD is Dinomaly (Guo et al., 2025), a reverse distillation architecture" by the authors. In fact, it is a reconstruction-based method. Given all these points, the reviewer keep the rating. [1] Zhang, Jiangning, et al. "Exploring plain vit reconstruction for multi-class unsupervised anomaly detection." arXiv preprint arXiv:2312.07495 (2023).

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

The paper presents an approach to industrial anomaly detection based on the established concept of reverse distillation. The authors build their work on the assumptions that unlabeled training dataset that are usually assumed to contain only normal data may also be contaminated with anomalies, which in turn affect training and standard reconstruction-based objectives to anomaly detection. To overcome this issue, they resort to positive unlabeled learning, where a small number of labeled examples is used to better separate anomalies from normal data. In this setting this is achieved through Otsu-based thresholding and adjusted learning objectives. The proposed approach is evaluated on one dataset and in comparison to a couple of competitors, where the proposed approach is reported as the top performer.

Critical strengths

The paper has several strengths that I can highlight:

  • The paper makes a good case for the approach and motivates the contribution to the family of reverse distillation methods to anomaly detection. While conceptually straight forward, the solution based on positive-unlabeled learning appears to be effective on the selected benchmark. It also outperforms the two selected competitors. The reported performance improvements are reasonably convincing.

  • The paper addresses a relevant industrial problem that is very timely and also actively researched. It is in general well written and easy to follow. The presented idea is sound and appears to work well in the studied setting. Ablation studies are presented to demonstrate the impact of the design choices and components. The paper also comes with supplementary material that presents additional results, both quantitative and qualitative.

Critical weaknesses

While I do find the paper interesting, I also have several concerns. Below are some that I feel are most critical:

  • The experiments are quite modest. All of the evaluations are conducted on a single dataset, which is typically not enough to demonstrate that the proposed solution generalizes to various settings. Kindly note that having experiments on a single dataset is already enough to reject a paper from any venue, even less demanding ones than ICLR. There are multiple datasets out there that could be used and appropriated for the studied setting, e.g., MVTech AD, but also others.

  • Also, beyond the dataset, the experimental evaluation would also need to be expanded in other areas. For example, to show that the PUL approach is general and not limited only to the Dinomaly backbone used in the paper. If this cannot be applied to other backbones and does not work as well, I would rate the novelty limited to a niche setting.

  • Another critical weakness in my view is the limited number of baselines included in the experiments. There are numerous methods out there for industrial anomaly detection and some of these may not be sensitive to contamination of the normal training data. Even under the studied setting, there are methods out there that have not been discussed or considered for the comparison, e.g., Dinomaly2 (only arxiv though), Memory-Distilled Selection (MeDS, ICML2026), etc.

  • It would be interesting to see how the model behaves with different contamination rates and different amounts of labeled data. This would help to better understand how much labeled data is needed to properly separate anomalies from normal data and how much or how little contamination the model can handle.

  • It is not completely clear how the proposed loss handles unlabeled data. If the main idea is to reduce the error in image areas that are more likely to contain anomalies, wouldn’t this increase the models capacity to reconstruct anomalies that are in the unlabeled set. This is the opposite of what the model wants to achieve with the labeled set. If the contamination level is high, the model would learn from conflicting learning objectives. A discussion on this would be needed in my view.

Questions for authors

I would welcome responses to questions related to the weaknesses highlighted above:

1.) Would it be possible to show that the proposed method generalizes beyond Real-IAD and the specific Dinomaly backbone?

2.) How competitive is the proposed method compared to recent contamination-robust anomaly detection approaches, such as MeDS (ICML 2026)?

3.) How sensitive is the proposed method to the contamination rate and the number of labeled anomalous samples?

4.) How does the approach prevent the model from learning to reconstruct anomalies in the unlabeled set, given that it explicitly minimizes reconstruction errors in potentially anomalous regions? A discussion on this would be welcomed.

2 comments

We thank the reviewer for the useful comments. In the following, we address the questions and the weaknesses.

Additional datasets (added to the Supplementary Material, Section "Additional quantitative results"). We added VisA (Table 6) and MVTec AD (Table 7), where our method also outperforms or is comparable to the selected baselines. This confirms that the gains are not specific to Real-IAD. Note that some MVTec AD categories contain only a small number of labeled anomalies, so the results on this dataset can be noisy.

Different backbone (added to the Supplementary Material, Section "Additional ablations"). We ran the full VisA benchmark with WideResNet50-2, the backbone of the original Reverse Distillation paper. It is a supervised CNN, fundamentally different from the self-supervised ViT (DINOv2) used by Dinomaly in both architecture and pretraining objective. With this backbone, our method gives no Image-AUROC gain, unlike with DINOv2. However, PRO improves by about 22 points (Table 12), indicating that the correction improves localization of the anomalous regions.

Comparison with MeDS (added to the Supplementary Material, Section "Additional quantitative results"). We evaluate MeDS on VisA using the same per-category PU split as for our method (Table 8). Our method outperforms MeDS on both image-level detection and localization. Moreover, the three-stage pipeline of MeDS took on average 2.12.1 hours per category, versus 2727 minutes per category for our method. This is consistent with the limitation stated by the MeDS authors themselves, i.e., "additional computational overhead".

Sensitivity to contamination rate and number of labeled anomalies. Please see our response to Reviewer z6cF (point "Sensitivity analysis"), where we run two controlled sweeps: one varying the contamination rate α\alpha, and one varying ∣P∣|\mathcal{P}|. In short, the advantage of our method over RD grows with the contamination rate, and grows with ∣P∣|\mathcal{P}| at a dataset-dependent rate.

Preventing the reconstruction of hidden anomalies (added to the main text, Section "Ablation study", "Defect separation analysis"). Following PU reasoning, we prevent it by including a filtering mechanism, that is, the hinge term LP,hinge\mathcal{L}_{\mathcal{P}, \text{hinge}}. Since images inside P\mathcal{P} are known with certainty to be anomalous, the hinge term explicitly pushes the flagged region's reconstruction error up, working against the push-down term's (LU\mathcal{L}_\mathcal{U}) tendency to decrease the error also on the hidden anomalous images in U\mathcal{U}. The ablations in the main text show that adding the hinge term (going from LU\mathcal{L}_U alone to LU+LP,hinge\mathcal{L}_U + \mathcal{L}_{P,\text{hinge}}) substantially increases detection (Image-AUC) and localization (PRO), confirming that hinge counteracts the contamination.

Empirically, we checked whether the contamination erases the defect/background distinction over training by tracking reconstruction error inside vs. outside the hidden ground-truth defect mask on Utrain\mathcal{U}_{\text{train}}, across VisA categories, comparing our method against a "no correction" variant (Fig. 3). We can observe, that both variants' separation grows over training rather than collapsing toward 11 (no separation). However, no-correction variant stays consistently smaller at every epoch, directly confirming that the hinge/anchor correction is what drive the larger separation, not just an accuracy-metric effect.

Additionally, the contamination sensitivity analysis (Fig. 4) shows that the performance gap between the model with and without this correction (Ours vs. RD) grows monotonically with the contamination rate, i.e., the correction's benefit scales with the severity of the underlying leakage, rather than being a fixed, marginal effect.

Reviewer_zTLkOpenReview ↗

Thank you!

I would like to thank the authors for their response and the effort put into the rebuttal. The updated manuscript now has results on MVTec AD and VisA, which is a plus. Additional baselines were also included, so was the analysis of the impact of the contamination rates and different amounts of labeled data. I feel that these efforts made the paper stronger.

However, I still have concerns that were not resolved properly. The first is about the generality of the proposed approach. The added experiment with the WideResNet50-2 backbone did not show as consistent improvements as with the Dinomaly backbone. While the authors report improvements in localization performance, there is no improvement in image-level anomaly detection with this backbone. This suggests that the effectiveness of the proposed objective may depend considerably on the underlying architecture and feature representation. This impacts the contribution quite a lot, as the method seems to be most useful with Dinomaly, so taking ideas from this work and applying it elsewhere may not be feasible or not bring the desired gains.

I also acknowledge the added analysis on how the loss affects the separation between defective and non-defective regions. While the results show that the objective works, I am not convinced that the results address my original concern about minimizing reconstruction errors in potentially anomalous regions of the unlabeled training data. The labeled anomaly samples appear to counteract this effect, but it is not completely clear to what extend this mechanism this generalizes.

In my view, the rebuttal has improved the paper and addressed several of my questions. Nevertheless, given the unresolved concerns, I will retain my original rating. If there was an option for Borderline, I would actually opt for that, but I feel this is not quite mature enough for a higher rating.

Reviewer_z6cFOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The submitted paper addresses the visual anomaly detection problem when the training set is polluted with anomalies at an unknown rate. Based on a reverse distillation the proposed method applies a threshold to each image’s error map to partition it into a flagged region and the others. Using a small, labeled set of anomalies, the method then pushes flagged region error up and the others down for labeled set of anomalies, and only pushes flagged-region error down corresponding to unlabeled images. The paper proposes a PU-style objective with a per-image threshold; designs an asymmetric loss without the requirement to know the contamination rate. Mean image AUROC performances rises from 0.869 to 0.928. Significance tests and ablations support the claim. However, only one dataset and backbone are considered.

Critical strengths
  • practical, well-posed setting
  • sensible asymmetric loss
  • consistent gains with statistics
Critical weaknesses
  • missing baselines
  • the theory and mechanism do not exactly match the proposed method
  • limited evaluation
Questions for authors
  • Eq. 4 drops the correction factor and the contamination-weighted anomaly term compared with Eq. 3. How is the loss positive-unlabeled, and how does it differ from anomaly exposure?
  • how do results change when one varies the contamination rate and also size of labeled set?
2 comments

We thank the reviewer for the useful comments. In the following, we address the questions and the weaknesses.

Is it a PU loss? Part of the loss is derived from the PU mixture in Eq. (2), so in this sense it can be considered a PU loss. We also add terms that are not directly derived from the mixture, to improve learning. This is common practice in other PU works. For example, nnPU (Kiryo et al., 2017) clips one term of the derived risk at zero to avoid overfitting, Dist-PU (Zhao et al., 2022) and VPU (Chen et al., 2020) similarly modify their derived objectives or add regularization terms to them, and more. Our hinge saturation and anchor term play a similar role.

Correction factor. Factors α\alpha and (1−α)(1 - \alpha) are hidden in Eq. (4). In particular, note that when the margin is not yet reached (R+(x)<mR^+(\mathbf{x}) < m), we have:

LU+β⋅LP,hinge=EEPu[R+(x)]+β⋅EPa[max⁡(0,m−R+(x))]=EPu[R+(x)]+β⋅EPa[m−R+(x)]=EPu[R+(x)]−β⋅EPa[R+(x)]+βm\begin{aligned} \mathcal{L}_\mathcal{U} + \beta \cdot \mathcal{L}_{\mathcal{P}, \text{hinge}} &\overset{\mathbb{E}}{=} \mathbb{E}_{P_u}[R^+(\mathbf{x})] + \beta \cdot \mathbb{E}_{P_a}[\max(0, m - R^+(\mathbf{x}))] \cr &= \mathbb{E}_{P_u}[R^+(\mathbf{x})] + \beta \cdot \mathbb{E}_{P_a}[m - R^+(\mathbf{x})] \cr &= \mathbb{E}_{P_u}[R^+(\mathbf{x})] - \beta \cdot \mathbb{E}_{P_a}[R^+(\mathbf{x})] + \beta m \end{aligned}

with =E\overset{\mathbb{E}}{=} being equality in expectation. Hence, for β=α\beta=\alpha, the first two terms differ from Eq. (3) only by a constant bias βm\beta m and a factor (1−α)−1(1 - \alpha)^{-1} (L267-268), and:

arg minθ LU+β⋅LP,hinge=Earg minθ (1−α)−1(EPu[R+(x)]−αEPa[R+(x)]).\mathop{\mathrm{arg\ min}}_\theta\ \mathcal{L}_\mathcal{U} + \beta \cdot \mathcal{L}_{\mathcal{P}, \text{hinge}} \overset{\mathbb{E}}{=} \mathop{\mathrm{arg\ min}}_\theta\ (1 - \alpha)^{-1}(\mathbb{E}_{P_u}[R^+(\mathbf{x})] - \alpha \mathbb{E}_{P_a}[R^+(\mathbf{x})]).

The factor (1−α)−1(1-\alpha)^{-1} is a positive constant and does not change the minimizer. The zeroing of the hinge term when it is saturated (R+(x)≥mR^+(\mathbf{x}) \ge m) and the addition of the anchor term are meant to improve the learning, in the ways explained in the paper (L264-268), and are not derived from the modeling of the PU equation.

Difference from outlier exposure. Outlier Exposure (OE) (Hendrycks et al., 2018) defines a general objective of the form EDin[L(f(x),y)]+λEDout[LOE(⋅)]\mathbb{E}_{D_{in}}[L(f(x),y)] + \lambda\mathbb{E}_{D_{out}}[L_{OE}(\cdot)], where the authors explicitly leave LOEL_{OE} as “a design choice” depending on the task. At this level of abstraction, the first two terms of Eq. (4) are indeed an instance of this template, and we will cite this line of work explicitly.

The difference is what DoutD_{out} and P\mathcal{P} actually are. In OE, DinD_{in} and DoutD_{out} are two separate, unrelated datasets, and DoutD_{out} is auxiliary data assumed disjoint from DinD_{in}: there is no claim that it is secretly mixed into it. In our setting, P\mathcal{P} is drawn from PaP_a, the same anomaly distribution already present, hidden, inside U\mathcal{U} itself: U\mathcal{U} and P\mathcal{P} are two views of the same contamination process, not two independent datasets.

In our method we start from a single explicit assumption, Eq. (2), that the pool we train on is itself a mixture, Pu(x)=(1−α)Pn(x)+αPa(x)P_u(x) = (1-\alpha)P_n(x) + \alpha P_a(x), for an unknown mixing weight α∈[0,1)\alpha\in[0,1). From this assumption alone we derive EPn[R+(x)]=(1−α)−1(EPu[R+(x)]−αEPa[R+(x)]).\mathbb{E}_{P_n}[R^+(\mathbf{x})] = (1-\alpha)^{-1}\Big(\mathbb{E}_{P_u}[R^+(\mathbf{x})] - \alpha\mathbb{E}_{P_a}[R^+(\mathbf{x})]\Big). We then show, as derived above, that the first two terms of Eq. (4) match this expression up to a positive factor and a constant.

We hope that this explanation makes the point you raised clearer, and we will include these considerations in the paper.

We thank the reviewer for the useful comments. In the following, we address the questions and the weaknesses.

Sensitivity analysis. To understand how the advantage of our method depends on the contamination of the unlabeled pool and on the amount of labeled data ∣P∣|\mathcal{P}|, we run two orthogonal controlled sweeps: one varies the contamination rate while keeping ∣P∣|\mathcal{P}| fixed, the other varies ∣P∣|\mathcal{P}| while keeping the contamination rate fixed. Fixing one factor while varying the other isolates each effect cleanly.

a) Contamination rate (added to the main text, Section "Ablation study").

Setting. We keep the test split Utest\mathcal{U}_{\text{test}} and the labeled pool P\mathcal{P} fixed, and change only the contamination rate α\alpha of the unlabeled pool Utrain\mathcal{U}_{\text{train}}. ∣P∣|\mathcal{P}| is fixed at 9090 per category on Real-IAD and at 3030 per category on VisA. We sweep the contamination rate over α∈0.05,0.1,0.2,0.3,0.4,0.5\alpha \in \\{0.05, 0.1, 0.2, 0.3, 0.4, 0.5\\} on Real-IAD and α∈0.1,0.2,0.3,0.4,0.5\alpha \in \\{0.1, 0.2, 0.3, 0.4, 0.5\\} on VisA. At each setting, we train and test both our method and an RD baseline (which has no contamination-correction mechanism) on identical data, so any difference between them at a given contamination rate is attributable to the correction mechanism itself.

Result. Fig. 4 plots Image-AUROC and PRO of our method and RD as a function of α\alpha on both datasets. The Image-AUROC gap between our method and RD grows monotonically with the contamination rate on both datasets. Both methods degrade as the unlabeled pool gets noisier, since more contamination makes the task harder for any method, but RD degrades faster: it has no mechanism to correct for contamination, while our method keeps compensating for it. The same pattern holds for PRO (localization): the gap grows monotonically with contamination on both datasets.

b) Number of labeled anomalies ∣P∣|\mathcal{P}| (added to the Supplementary Material, Section "Additional ablations").

Setting. We keep the training set Utrain\mathcal{U}_{\text{train}} and the test set Utest\mathcal{U}_{\text{test}} identical across all values of ∣P∣|\mathcal{P}| (by reusing the construction of the largest ∣P∣|\mathcal{P}|), with a fixed contamination rate (α=0.2\alpha=0.2 on VisA, α=0.3\alpha=0.3 on Real-IAD). We vary ∣P∣∈5,10,20,30,40|\mathcal{P}| \in \\{5, 10, 20, 30, 40\\} on VisA and ∣P∣∈5,20,50,150|\mathcal{P}| \in \\{5, 20, 50, 150\\} on Real-IAD. At each setting, we train and test both our method and an RD baseline (which never uses P\mathcal{P}) on identical data, so any difference between them at a given ∣P∣|\mathcal{P}| is attributable to how much our method benefits from P\mathcal{P}, not to a difference in training data.

Result. Fig. 8 plots Image-AUROC and PRO of our method and RD as a function of ∣P∣|\mathcal{P}| on both datasets. The Image-AUROC gap between our method and RD grows with ∣P∣|\mathcal{P}| on both datasets, but at different rates: on VisA the gap is already visible at ∣P∣=20|\mathcal{P}|=20, while on Real-IAD it appears later, around ∣P∣=50|\mathcal{P}|=50. The PRO (localization) gap stays roughly flat across ∣P∣|\mathcal{P}| on VisA, while on Real-IAD it grows slightly at low ∣P∣|\mathcal{P}|. We attribute this difference to the acquisition conditions of the two datasets. In VisA, anomalies vary little beyond the defect itself (camera, lighting, and pose are fixed per category), so a few labeled examples already cover a large part of that limited variation. Real-IAD is more varied, with many more anomaly instances per category, so the same ∣P∣|\mathcal{P}| covers a thinner slice of that variation, and more labeled anomalies are needed to generalize.

Missing baselines and limited evaluation. We added new baselines (LOE, SOEL, MeDS), evaluation on new datasets (VisA, MVTec AD), and additional ablations. Our method remains the best or comparable in all settings:

  • LOE and SOEL are added on Real-IAD (Table 1).
  • The comparison is extended to VisA and MVTec AD (Tables 6 and 7).
  • A MeDS baseline is added on VisA (Table 8).

We also ran several auxiliary analyses that validate our design choices: Otsu split vs. a fixed top-kk selection and an alternative backbone (Supplementary Material, Section "Additional ablations"), and a defect separation analysis (main text, Section "Ablation study").

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.