acceptodds
Under review as a conference paper at ICLR 2027

Micro-Defects Expose Macro-Fakes: Detecting AI-Generated Images via Local Distributional Shifts

Abstract

Recent generative models can produce images that appear highly realistic, raising challenges in distinguishing real and AI-generated images. Yet existing detectors based on pre-trained feature extractor tend to over-rely on global semantics, limiting sensitivity to the critical micro-defects. In this work, we propose Micro-Defects expose Macro-Fakes (MDMF), a local distribution-aware detection framework that amplifies micro-scale statistical irregularities into macro-level distributional discrepancies. To avoid localized forensic cues being diluted by plain aggregation, we introduce a learnable Patch Forensic Signature that projects semantic patch embeddings into a compact forensic latent space. We then use Maximum Mean Discrepancy (MMD) to quantify distributional discrepancies between generated and real images. Our theory-grounded analysis shows that patch-wise modeling yields provably larger discrepancies when localized forensic signals are present in generated images, enabling more reliable separation from real images. Extensive experiments demonstrate that MDMF consistently outperforms baseline detectors across multiple benchmarks, validating its general effectiveness.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI-Generated Images Detection, Patch Forensic Signature

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_xMM7OpenReview ↗
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2
Confidence
4
Informativeness
2
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2
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Paper summary

Existing AI-generated image detectors tend to over-rely on global semantics, limiting sensitivity to the critical micro-defects. To address this issue, this paper proposes Micro-Defects expose Macro-Fakes (MDMF), a local distribution-aware detection framework that amplifies micro-scale statistical irregularities into macro-level distributional discrepancies. Furthermore, the authors introduce a learnable Patch Forensic Signature to avoid localized forensic cues being diluted by plain aggregation. Then they use Maximum Mean Discrepancy (MMD) to quantify distributional discrepancies between generated and real images. A theoretical analysis shows that the patch-wise modeling yields provably larger discrepancies. Extensive experiments demonstrate the effectiveness of the proposed method across multiple benchmarks.

Critical strengths
  1. Well-motivated problem. The authors state that local micro-defects matter in AI-generated image detection task, which is coherent with common sense and widely recognized by related area.
  2. Theoretical proof. The authors provide a theoretical analysis in sec 2.4 to support their proposed method, which should be beneficial.
  3. Experiments on generated videos. The authors conduct further experiments on generated videos in Fig.3, which further demonstrate the effectiveness of the proposed method.
  4. This paper is well-organized and easy to follow.
Critical weaknesses
  1. Intuition novelty. Although I acknowledge this paper's intuition that local artifacts matter, this has been widely recognized in this area, and I believe there are already enough works proposed based on this intuition. More discussions on the differences with these works are needed. It is truly hard to say 'a new perspective' as the authors stated in the contribution part.
  2. Technique novelty. Although I acknowledge the effectiveness of the proposed method, it involves many existing techniques, such as DINOv2, MMD, local patch learning. More justifications of the technique novelty are required.
  3. Theoretical proof. The analysis depends on restrictive assumptions. Will it still work under more general real-world settings? And does the theoretical theorem 2.7 still hold for single image inference? Besides, I think the performance should be highly related to the images chosen as reference set, did the authors conduct further analysis on this?
  4. More realistic and advanced generators. The proposed method performs well on the chosen benchmarks. However, the tested generators are somewhat old. With the generators still evolving, the generated image may be more realistic and have no recognizable local artifacts. Did the authors test on more recent and stronger generators? This should provide more support for their proposed method's superiority.
Questions for authors

Please see the weakness above. My major concerns focus on the novelty, theoretical analysis, and generalization under stronger generators. Thus, I currently lean towards a negative rating.

3 comments
AuthorsOpenReview ↗

[1/3] Rebuttal by Authors

Thank you for your time and constructive review. Here are our detailed replies.

W1 & W2: Novelty of the intuition and of the technique

R1: Thanks for the constructive comments. Section 2.3 builds on the deep-kernel test of [1] and the reference-based scoring of [2, 3], and Appendix C discusses patch-level classifiers [4] and PatchCraft [5], while a direct comparison of their design choices with MDMF was missing. We would like to reclaim that our work is novel in introducing a patch-level formulation of single-image detection, i.e., comparing the field of patch forensic signatures of one image with the fields of a population of real references. This has not been explored in previous local-artifact detectors [4–6], and has both conceptual and technical distinctions from them with significant knowledge advancement.

Conceptually, the local-artifact detectors [4–6] map local evidence to a real/fake decision with a trained classifier, whereas MDMF scores a test image by how far the field of its local evidence departs from the fields of real reference images. The table below summarizes the differences.

MethodLocal evidenceImage-level decisionTraining objectiveReal references at testAUROC in Table 1
Chai et al. [4]Patch logits of a truncated CNNAverage of patch predictionsPatch-wise cross-entropyNo–
PatchCraft [5]Rich- and poor-texture contrastCNN classifierBCENo86.13
NPR [6]Neighboring-pixel relationsCNN classifierBCENo86.00
MMD-MP [2] (text), NSG-VD [3] (video)Token or frame featuresDeep-kernel MMD to real referencesMulti-population-aware MMD objectiveYes–
MDMFPFS field of frozen DINOv2 patchesDeep-kernel MMD to real referencesMMD test power on PFS fieldsYes95.65

Technically, MDMF differs from the local-artifact detectors [4–6] in three aspects, and the first aspect also distinguishes MDMF from the deep-kernel MMD methods [1–3].

① Scalar patch signatures. A shared head maps each of the 49 pooled patch embeddings of an image to a scalar PFS, and the image is represented by the field of these signatures without image-level pooling or voting, whereas [1] uses a generic vector featurizer and [2, 3] use token or frame features.

② Test power on the patch field. The PFS head and the kernel are trained with the test-power objective of [1] on the fields of real and generated images (Eq. 5), whereas the local-artifact detectors [4–6] are trained with classification losses.

③ Scoring against real references. A test image is scored by the MMD between its field and a bank of real images (Eq. 6), whereas [4–6] score the image with a trained classifier.

Empirically, with the same frozen backbone and training data, an MMD objective on a global image-level output lowers the AUROC from 90.14 to 86.53, whereas the MMD objective of MDMF on the PFS field raises the AUROC from 93.22 to 95.65 (Table 2), which shows that the gain of the MMD objective depends on the PFS field. Direct combinations of DINOv2 with local patch learning or MMD also stay below the five-run average of MDMF (94.97, Table 10), namely pooling the patch signatures (at most 93.22, Table 7), classifying each patch and voting (at most 94.43 even with the best of eight patch thresholds, Table 16) and a generic deep-kernel featurizer on the same patches (91.87, Table 9). We have replaced "a new perspective" in the contribution statement of Section 1 with the patch-level formulation above, revised the first sentence of the conclusion accordingly, and added the comparison table to Appendix C.

[1] Learning Deep Kernels for Non-Parametric Two-Sample Tests. ICML 2020

[2] Detecting Machine-Generated Texts by Multi-Population Aware Optimization for Maximum Mean Discrepancy. ICLR 2024

[3] Physics-Driven Spatiotemporal Modeling for AI-Generated Video Detection. NeurIPS 2025

[4] What Makes Fake Images Detectable? Understanding Properties that Generalize. ECCV 2020

[5] PatchCraft: Exploring Texture Patch for Efficient AI-generated Image Detection. arXiv 2023

[6] Rethinking the Up-Sampling Operations in CNN-based Generative Network for Generalizable Deepfake Detection. CVPR 2024

AuthorsOpenReview ↗

[2/3] Rebuttal by Authors

W3a: Restrictive assumptions and more general settings

R2: Thanks for this insightful question. The Gaussian surrogate in PFS space provides the closed form of Proposition 2.6, and Appendix B.4 already notes that the Gaussian kernel gives a positive MMD whenever the distributions of the PFS fields differ. The random sign in Assumption 2.3 describes defects without a preferred direction, which is the regime in which Proposition 2.5 shows that pooling attenuates the shift. The positivity of the population MMD and the separation in Corollary B.4 hold for any defect distribution that shifts the mean PFS, as shown below.

Theoretically, ① let a defective patch have embedding u+δ\mathbf u+\boldsymbol\delta, where δ\boldsymbol\delta follows any distribution and may depend on u\mathbf u, the defect indicator a∼Bernoulli(ρ)a\sim\mathrm{Bernoulli}(\rho) is independent of (u,δ)(\mathbf u,\boldsymbol\delta), and u\mathbf u has the same distribution for real and generated images. Then the PFS mean shift has the exact form ΔPFS=ρ E[ϕθ(u+δ)−ϕθ(u)]\Delta_{\mathrm{PFS}}=\rho\,\mathbb E[\phi_\theta(\mathbf u+\boldsymbol\delta)-\phi_\theta(\mathbf u)]. Assumption 2.3 is the special case of this defect model with δ=sμdefect\boldsymbol\delta=s\boldsymbol\mu_{\mathrm{defect}}.

② A nonzero ΔPFS\Delta_{\mathrm{PFS}} shifts the mean of the PFS field, so real and generated images induce different field distributions. Since the Gaussian kernel of Eq. 4 is characteristic on the field space, the population MMD is positive without the Gaussian surrogate.

③ Lemma B.3 requires only i.i.d. samples and a bounded kernel that is fixed independently of them, so Corollary B.4, whose condition involves only the population MMD, separates sets of real and generated test images whenever this MMD exceeds twice the finite-sample term.

Empirically, computing the PFS of every patch before pooling improves over the global-pooling baseline on the same frozen backbone under the same BCE objective (93.22 vs. 90.14 AUROC, Table 2), in line with Proposition 2.5. The shift in ① is also measurable, since ΔPFS\Delta_{\mathrm{PFS}} is the difference between the mean PFS of generated and real patches. On the ImageNet test set, this shift is nonzero for all nine generators under each of the five trained heads with W = 32 in Table 10, and none of the 45 image-level bootstrap 95% confidence intervals contains zero. We have added this generalization to Appendix B and the measured shifts to Appendix E.4.

W3b: Theorem 2.7 and single-image inference

R3: Thanks for this important question. We would like to first clarify that the single-image score of Eq. 6 is analyzed by Proposition B.5 in Appendix B.5, while Theorem 2.7 is stated for sets of test images and does not directly apply to a single image. Theorem 2.7 uses the unbiased MMD estimator, which requires at least two test images, whereas Eq. 6 uses the biased estimator with one test image. For a real image yry_r and a generated image ygy_g with a positive population similarity margin m(yr,yg)=EX∼P[kω(X,yr)−kω(X,yg)]m(y_r,y_g)=\mathbb E_{X\sim\mathbb P}[k_\omega(X,y_r)-k_\omega(X,y_g)], Proposition B.5 shows that a bank of RR real references assigns the higher score to ygy_g with probability at least 1−exp⁡(−Rm2/2)1-\exp(-Rm^2/2). The ordering of two test images is therefore determined by their margin and becomes insensitive to the sampled references as RR grows. Consistently, replacing the reference bank with other ImageNet images changes the average AUROC by at most 0.01 (see R4). We have revised the case labels and the interpretation of Theorem 2.7 in Section 2.4 so that they refer to sets of test images and point to Proposition B.5 for the single-image score.

AuthorsOpenReview ↗

[3/3] Rebuttal by Authors

W3c: Dependence on the reference set

R4: Thanks for raising this point. We would like to first claim that we have varied the reference size from 1k to 10k (Table 12 in Appendix E.7) and replaced the ImageNet references with LSUN-Bedroom images, with little change in either case. To further examine the composition of the reference set, we keep the five trained heads with W = 32 in Table 10 fixed and replace only the reference bank, which all five heads share in the paper. We draw ten new disjoint 3k banks from ImageNet training images, restrict the bank to 30 or 300 classes, compress the references with JPEG, and use 1,750 MSR-VTT video frames as a cross-domain bank. Cells report average AUROC and AP over the five heads (mean±std in the first two rows and the last row).

Reference setAUROCAP
Paper bank (3k ImageNet images)94.97±0.4596.65±0.27
Ten new 3k ImageNet banks94.97±0.4496.65±0.27
30 / 300 classes94.98 / 94.9796.65 / 96.65
JPEG references (q = 75)94.9796.64
MSR-VTT frames (cross-domain)93.93±1.7696.08±0.95

Within the ImageNet domain, the average AUROC stays within 0.01 of the paper bank, and for a fixed head the standard deviation across the eleven random banks is 0.009 on average. This stability agrees with Proposition B.5, since the ordering of two test images is set by their margin once the bank is large enough. The 30-class bank also performs like the 300-class bank, in line with the reduced category decodability of the learned patch representation (Table 8). A bank of video frames from another domain lowers the average AUROC by about 1.0, so real references from the target domain are preferable under a large domain change. On ImageNet, a bank of 1k such references already performs like one of 10k (Table 12). We have added this analysis to Appendix E.7 and updated the discussion of the reference set in Appendix E.7 and Appendix G with these results.

W4 (Q): More recent and stronger generators

R5: Thanks for this question. Following your suggestion, we evaluated MDMF on X-AIGD [7], a recent benchmark with 13 text-to-image generators including FLUX.1-dev, SD 3.5 Large and Infinity. Its labeled test split contains 2,419 generated images paired with 1,290 real images, and 1,168 of these real images can still be retrieved in their original form. As noted in [7], the generated images are PNG files while the real images are mostly JPEG files. To prevent the file format from separating the two classes, we use the compression fields provided by [7] and compress each generated image with the JPEG quality and chroma subsampling of its paired real image. MDMF uses 1,743 real images of the X-AIGD training split as its reference. AIDE and Effort are trained on the same data as MDMF with their official code (configurations in Appendix D.3). Cells report average AUROC over the 13 generators, and the ProGAN row of MDMF reports mean±std over the five runs with W = 32 in Table 10.

Training dataMDMFAIDEEffort
ProGAN (same in Table 1)54.24±0.8147.9937.16
SD v1.4 (same in Figure 3)85.2872.1781.02

With ProGAN training, all three detectors are close to or below chance on these generators, and MDMF obtains the highest AUROC of the three. The X-AIGD paper [3] also reports near-chance accuracy (48.6% to 52.1%) for the ProGAN-trained CNNspot, UnivFD and FatFormer. With SD v1.4 training, MDMF still outperforms AIDE and Effort. We have added these results, together with those on the published files without compression alignment, to Appendix E.1.

[7] Unveiling Perceptual Artifacts: A Fine-Grained Benchmark for Interpretable AI-Generated Image Detection. arXiv 2026

Reviewer_zQPhOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

The paper introduces MDMF, a detection framework that identifies AI-generated images by focusing on local irregularities/micro-defects as opposed to semantic cues. The authors argue that modern generative models are great at creating convincing images at a macro level, making global detectors unreliable. To address this, the method utilizes a DINOv2 encoder to extract fine-grained patch-level features, avoiding any patch-level aggregation which could lose this local information. They propose Patch Forensic Signature (PFS), a patch-wise projection function which is is then trained to maximize the Maximum Mean Discrepancy (MMD) between real and fake patch distributions. The claim is that this PFS-based method learns to use micro-artifacts instead of macro-semantic ones. This approach demonstrates good performance across various benchmarks (ImageNet, OpenSORA, GenImage, and LSUN bedroom). Ablations study robustness to backbone choice as well as robustness to post-processing. There is also an ablation comparing the design choice of patch wise MMD vs patch wise classification and also certain other aggregation techniques.

Critical strengths

I agree with the motivation presented, which is not relying only on global semantic cues. The results are shown on 4 benchmarks, against a lot of baselines which is evidence that the method works. Ablations also show that the method demonstrates good robustness to design choices such as encoder-choice as well as certain post-processing operations.

Critical weaknesses
  1. I would like to see more convincing evidence for the detector actually looking at localized and sparse evidence. To my understanding, local evidence is something which can be present in multiple patches of the image, but it is a pattern which is restricted to a patch region, as opposed to involving the whole image. Sparse evidence is a case where the image is mostly real while very small regions are generated. Based on these definitions, the only evidence that I currently see for sparse evidence, is the qualitative example in Fig. 5. I have the following concerns and suggestions for this experiment, (a). Other than the zebra example (with a blurry leg), I am unable to understand the defects identified in the other examples. (b). The authors argue that MDMF focuses on a sparse evidence, whereas the global pooling baseline focuses on "global" evidence. Firstly it is not clear if the generated images only contain sparse evidence (which is being interpreted as a positive signal in this case). Secondly, it is also not clear if global pooling baseline is looking for semantic details (for instance, localized evidence could manifest as subtle granular traces in every patch of the image, and the global model could be focusing on that). In fact several models [1,2] train on just 96x96 crop of generated image, the fact that they work decently shows that these images contain generative traces everywhere but these are also not global patterns (since even small crops carry that signal).

Based on this I suggest the following experiment to better understand the same, the authors need to guarantee that there are only sparse artifacts in the image (and obtain some quantitative results), hence I would prefer seeing a case where they test on a real image has been partially modified with generative model (i would also like to see AP, instead of qualitative results only), to the best of my knowledge [2,3] have this kind of experiment in Sec 5.4 (in both, in AEROBLADE it says Localized Inpainted Regions), however the authors are free to create/find these kind of settings to run this experiment. This will give me confidence as to whether given a situation with sparse artifacts, these benefits accurately transfer.

For localized artifacts, I would like to see more convincing evidence that MDMF specifically relies on local forensic cues rather than semantic information. One possible experiment would be to consider images where multiple patches independently contain detectable generative artifacts, potentially verified using detectors trained on small crops, such as [1, 2]. The authors could then examine whether MDMF highlights these regions, while the global pooling baseline instead focuses on semantically meaningful regions. This would help substantiate the claim that the two methods rely on fundamentally different types of evidence.

I acknowledge that GradCAM may not be sufficient to conclusively establish this distinction, and I cannot think of a more definitive experiment at the moment. I am therefore open to alternative experimental designs from the authors that convincingly demonstrate that MDMF relies on localized forensic evidence, whereas global pooling predominantly exploits semantic information.

  1. Some of the robustness experiments, such as robustness to backbone design as well as post-processing operations only compare with a single baseline (F-ConV). While it is difficult to expect comparisons with every single baseline on every experiment, I would like to understand why F-ConV in particular was chosen. Without understanding this, or seeing comparisons with stronger detectors (as per ImageNet benchmark such as AIDE and Effort), it is hard to know if these claims are meaningful.

  2. Lines 363-366 make the claim that performance on "recent" generative models indicates that the model is focusing on microscoping details. This claim would be reasonable if the models were more recent. In Table 1 as well as OpenSora, all the baselines are atmost 2024, which is somewhat outdated based on the speed of development. I thereby request the authors to evaluate their technique on modern benchmarks such as [4].

References,

  1. Corvi, Riccardo, et al. "On the detection of synthetic images generated by diffusion models." ICASSP 2023-2023 IEEE International Conference on Acoustics, Speech and Signal Processing (ICASSP). IEEE, 2023.
  2. Rajan, A. S., & Lee, Y. J. (2025). Stay-positive: A case for ignoring real image features in fake image detection. arXiv preprint arXiv:2502.07778.
  3. Ricker, J., Lukovnikov, D., & Fischer, A. (2024, June). Aeroblade: Training-free detection of latent diffusion images using autoencoder reconstruction error. In 2024 IEEE/CVF Conference on Computer Vision and Pattern Recognition (CVPR) (pp. 9130-9140). IEEE.
  4. Xiao, Y., Chen, W., Chen, J., Cao, Z., Deng, W., Yang, B., ... & Lin, L. (2026). Unveiling Perceptual Artifacts: A Fine-Grained Benchmark for Interpretable AI-Generated Image Detection. arXiv preprint arXiv:2601.19430.

Currently, the only evidence shown for the attention to local detail is the qualitative examples in Fig. 5 (i also have some concerns here which I will state later). The authors mention modern generative models leave localized and sparse evidence, however, it the qualitative examples are at-based an example of sparse evidence. Localized evidence to the best of my understanding

Questions for authors
  1. OpenSora bench in Fig.3 is developed by the authors to the best of my knowledge, if so why were detectors such as AIDE and Effort, which seem to do the best on ImageNet (barring the MDMF) used in this evaluation? It would be helpful to see the numbers.
  2. If the authors wanted to not rely on local-semantic evidence (which seems reasonable to me), why start with DINO in the first place? The attention operation would certainly leak information between patches.
5 comments
AuthorsOpenReview ↗

[1/3] Rebuttal by Authors

Thank you for your detailed and constructive review. Here are our detailed replies.

W1a: Sparse evidence and the examples in Figure 5

R1: Thanks for the precise definitions of local and sparse evidence. We would like to first clarify the meaning of sparsity in our paper. Assumption 2.3 describes a fully generated image in which each patch deviates from real patches with probability ρ\rho, so sparsity refers to the spatial support of the detectable deviations within a generated image. A mostly real image with a small generated region is a controlled case of this setting, and we evaluate this case in R2 (W1b). Under Assumption 2.3 and Proposition 2.4, Proposition 2.5 shows that keeping the field of patch signatures preserves a larger leading-order shift than pooling the patch embeddings into one global representation.

Regarding (a), the MDMF heatmaps of Figure 5 show where the PFS responses are strongest, and they do not establish that the highlighted regions are verified defects. We have revised the caption of Figure 5 and the corresponding text in Section 3.3 and Appendix F to present the heatmaps as qualitative patterns of local responses.

Regarding (b), MDMF does not require the generated images to contain only sparse evidence, since the MDMF score (Eq. 6) compares the whole field of 49 patch signatures with the real reference, so deviations spread over many patches also contribute. We compare the evidence used by MDMF and by global pooling quantitatively in R3 (W1c).

W1b: Partially generated images, with AP

R2: Thanks for this valuable suggestion. Similar to the partially inpainted images in Stay-Positive [1] and AEROBLADE [2], our test images are real photos in which only one region is regenerated. For each setting, we take 500 COCO val2017 photos (center-cropped and resized to 512×512) and inpaint one region with SD 1.5 Inpainting or SDXL Inpainting, using a rectangle or a COCO object mask that covers about 3%, 10%, 25% or 50% of the image and the caption of the photo as the prompt. All pixels outside the mask are copied back from the original photo, so only the masked region is generated. The negatives are the same 500 photos, so both classes share content, resolution and file format. We compare MDMF with the global-pooling baseline of Table 2 (Global-BCE), which uses the same frozen DINOv2 ViT-L/14. Both are the ProGAN-trained models of the paper, MDMF keeps the ImageNet reference set of Table 1, and neither model is retrained or tuned on inpainted images. Cells report AP (%) of MDMF / Global-BCE (chance level 50%).

Inpainting model, mask3%10%25%50%
SD 1.5, rectangle51.5 / 50.769.9 / 51.979.2 / 54.286.5 / 58.3
SD 1.5, object52.2 / 51.970.4 / 53.379.9 / 55.786.9 / 61.3
SDXL, rectangle52.1 / 50.767.7 / 51.877.5 / 53.686.3 / 56.6
SDXL, object51.9 / 51.765.5 / 52.576.4 / 54.883.6 / 59.0

The advantage of MDMF over global pooling in Table 2 carries over to partially generated images. MDMF obtains a explicit higher AP in all the 16 settings, and on average the gap grows with the edited area from 0.7 to 29.7 AP. When the edited region covers about only 3% the image, i.e., about 1 of the 49 patches, both detectors stay close to chance. We have added this experiment to Appendix E.12.

[1] Stay-Positive: A Case for Ignoring Real Image Features in Fake Image Detection. ICML 2025

[2] AEROBLADE: Training-Free Detection of Latent Diffusion Images Using Autoencoder Reconstruction Error. CVPR 2024

AuthorsOpenReview ↗

[2/3] Rebuttal by Authors

W1c: Local forensic cues versus semantic information

R3: Thank you for being open to alternative designs. First we would like to clarify that the paper already provides two quantitative analyses of semantic reliance. In the label-inversion test of Figure 1, reversing the pairing between object category and real/fake label lowers the AUROC of the global detector by 39.9 points and that of the PFS model by 1.0 point. The linear probes of Table 8 show that the object category is much less decodable from the MDMF patch representation than from the DINOv2 patch features (46.65% vs. 83.52% with 20 classes), while the real/fake information is preserved (97.88% vs. 97.50%).

To compare the evidence used by the two detectors without heatmaps, we further measure how much of each detector score is explained by image semantics. Every ImageNet test image belongs to one of 1,000 classes. Within each test set, we compute the fraction of the variance of the score ranks that is explained by the class (the correlation ratio η2\eta^2) and subtract the same fraction computed with randomly shuffled classes (0.01 to 0.02). A detector whose score follows semantic content yields a large fraction. Cells report this fraction on the 50,000 real test images and its average over the nine generated test sets (MDMF: mean±std over the five runs with W = 32 in Table 10).

Test imagesMDMFGlobal-BCE
Real0.220±0.0270.398
Generated (average of 9)0.264±0.0040.370

The image class explains a smaller part of the MDMF score than of the global-pooling score on both real and generated images, which shows that the MDMF score depends less on semantic content. R2 complements this analysis with real and partially generated photos that share content, resolution and file format. We have added this analysis with the per-generator values to Appendix E.4.

W2: Choice of F-ConV, and comparison with AIDE and Effort

R4: Thanks for raising this point. We chose F-ConV because it is built on DINOv2 that is same as MDMF, so both methods can be instantiated with the same four DINOv2 encoders from ViT-S to ViT-G in the backbone study (Figure 4(b), Table 11), and F-ConV is among the strongest baselines of Table 1. AIDE (ICLR 2025) and Effort (ICML 2025) are built on other backbones, an OpenCLIP ConvNeXt-XXL and a CLIP ViT-L/14 with SVD-based fine-tuning.

Following your suggestion, we further evaluated AIDE (with its official ConvNeXt-XXL backbone) and Effort under the perturbations of Figure 4(c) on the full ImageNet test sets. Both are trained on the same four-class ProGAN data with the configurations used in Table 1 (Appendix D.3). Cells report average AUROC / AP (%) over the nine generators at the mildest, middle and strongest of the five severity levels.

PerturbationMDMFAIDEEffort
JPEG, q = 9094.32 / 96.2986.49 / 90.3676.68 / 85.10
JPEG, q = 7092.58 / 95.2482.40 / 87.6068.71 / 79.18
JPEG, q = 5091.39 / 94.4878.66 / 84.7066.73 / 77.51
Blur, σ = 195.30 / 96.8587.61 / 91.1990.64 / 94.14
Blur, σ = 391.10 / 93.7975.52 / 81.5568.77 / 77.33
Blur, σ = 581.21 / 85.5565.90 / 72.7759.00 / 67.49
Noise, σ = 0.0591.75 / 94.7382.19 / 87.1877.96 / 85.96
Noise, σ = 0.1587.39 / 91.5873.84 / 79.3671.80 / 78.99
Noise, σ = 0.2581.76 / 86.9355.33 / 64.6263.17 / 71.14

MDMF achieves the highest AUROC and AP at every severity level of the three perturbations, and its margin over both detectors is larger at the strongest level than at the mildest one. We have added the results of AIDE and Effort at all five severity levels to Appendix E.8.

AuthorsOpenReview ↗

[3/3] Rebuttal by Authors

W3: Recent generators and evaluation on X-AIGD

R5: Thanks for this suggestion. Following your suggestion, we evaluated MDMF on the labeled test split of X-AIGD [3], which contains 2,419 generated images from 13 text-to-image generators including FLUX.1-dev, SD 3.5 Large and Infinity, and their paired real images, of which 1,168 out of 1,290 can still be retrieved in their original form. As noted in [3], the generated images are PNG files while the real images are mostly JPEG files. To prevent the file format from separating the two classes, we use the compression fields provided by [3] and compress each generated image with the JPEG quality and chroma subsampling of its paired real image. MDMF uses 1,743 real images of the X-AIGD training split as its reference. AIDE and Effort are trained on the same data as MDMF with their official code (configurations in Appendix D.3). Cells report average AUROC over the 13 generators, and the ProGAN row of MDMF reports mean±std over the five runs with W = 32 in Table 10.

Training dataMDMFAIDEEffort
ProGAN (same in Table 1)54.24±0.8147.9937.16
SD v1.4 (same in Figure 3)85.2872.1781.02

With ProGAN training, all three detectors are close to or below chance on these generators, and MDMF obtains the highest AUROC of the three. The X-AIGD paper [3] also reports near-chance accuracy (48.6% to 52.1%) for the ProGAN-trained CNNspot, UnivFD and FatFormer. With SD v1.4 training, MDMF still outperforms AIDE and Effort. We have added these results, together with those on the published files without compression alignment, to Appendix E.1.

Q1: AIDE and Effort on OpenSora

R6: Thanks for this question. We would like to first clarify that the OpenSora test set is sampled from public data and is not generated by us. The generated frames come from the OpenSora subset of the GenVideo benchmark [4], and the real frames come from MSR-VTT [5] (Appendix D.1). Following your suggestion, we evaluated AIDE and Effort on the same 32,750 generated and 32,750 real frames. Both are trained with their official code on the same SD v1.4 training set as MDMF (configurations in Appendix D.3). Cells report AUROC / AP (%).

MethodAUROC / AP
F-ConV (best baseline in Figure 3)88.87 / 85.81
AIDE86.21 / 83.59
Effort91.04 / 91.18
MDMF92.93 / 92.99

MDMF outperforms AIDE, Effort, and the eight baselines of Figure 3. We have added AIDE and Effort to Figure 3 and revised the discussion of the OpenSora case study in Section 3.2 to include these results.

[4] DeMamba: AI-Generated Video Detection on Million-Scale GenVideo Benchmark. arXiv 2024

[5] MSR-VTT: A Large Video Description Dataset for Bridging Video and Language. CVPR 2016

Q2: Choice of DINOv2 given cross-patch attention

R7: Thanks for this insightful question. MDMF does not require the DINOv2 patch tokens to be free of semantic content or isolated from each other. As stated in Sections 2.1 and 2.2, the DINOv2 patch embeddings remain largely semantics-oriented, and PFS is introduced to map them into a forensic space that deemphasizes semantic variation. We start from frozen DINOv2 because its patch tokens preserve fine spatial information, as shown by dense prediction tasks such as depth estimation [6], and because frozen pre-trained features generalize well across generators, as shown by Ojha et al. (CVPR 2023). Self-attention mixes information across patches, and MDMF only requires the patch tokens to retain forensic information that a single global representation dilutes.

On the same frozen backbone, modeling the patch tokens outperforms the global-pooling baseline under both objectives of Table 2. PFS is trained only for real/fake discrimination, yet the object category becomes much less decodable from the MDMF patch representation while the real/fake information is preserved (Table 8), and the MDMF score depends less on the image class than the global baseline (R3).

[6] DINOv2: Learning Robust Visual Features without Supervision. TMLR 2024

Reviewer_tNP3OpenReview ↗
Rating
2(−1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes MDMF for cross-generator AI-image detection. A frozen DINOv2 encoder supplies patch tokens, which a shared MLP maps to scalar Patch Forensic Signatures. A Gaussian kernel over the resulting feature fields is trained using a variance-normalized MMD objective. Each test image is then scored against real references using biased MMD. Evaluation covers ImageNet, LSUN-Bedroom, GenImage, and OpenSora frames, with extensive supplementary analyses.

Critical strengths
  • The complete configuration provides a meaningful gain over a strong internal control: with the same frozen DINOv2 backbone, Table 7 reports 95.65 mean AUROC versus 93.22 for PFS-Attn-BCE. Table 1 also improves over F-ConV from 93.77/93.38 to 95.65/97.07 AUROC/AP. This supports a useful empirical contribution even without a new MMD objective.
  • The evaluation goes beyond a single headline result. Table 10’s five W=32 runs average 94.97 AUROC, and the appendix includes alternative pooling, a vector deep-kernel control, multiple backbones, reference-bank checks, and B-Free/DDA combinations. These support the configuration’s utility, although they are not a matched multi-seed significance comparison against all baselines. The paper also discusses false positives and qualifies confounded comparisons.
Critical weaknesses
  • The theoretical and mechanistic claims need correction. Proposition 2.4’s nonzero-shift conclusion does not follow from a nonzero Hessian quadratic form alone. For example, u=0u=0, μ=1\mu=1, and ϕ(t)=t2(1−t2)\phi(t)=t^2(1-t^2) give a nonzero quadratic term but zero actual mean shift. A condition controlling the Taylor remainder, consistent with the bound in B.2, is needed. Also, Eq.4 compares spatially ordered feature fields, and the heatmaps in D.3 do not establish that the final scores localize verified defects. These limitations narrow the mechanism claim but do not invalidate the observed empirical gains. Deep-kernel training and reference MMD are established components [A–C]; the contribution is their effective specialization here.
  • The GenImage and robustness comparisons need protocol clarification. D.2–D.3 describe evaluation-optimal ACC thresholds, but Table 5 includes imported results such as CNNspot’s 39.8 ACC on GLIDE, which cannot be optimal over all thresholds. F-ConV’s mean AUROC is also 93.77 in Table 1, 91.25 at zero blur in Table 14, and 91.00 at zero noise in Table 15, while MDMF stays at 95.65. These discrepancies weaken the auxiliary comparisons. The current evidence does not establish that they also affect Table 1 or Table 7.
Questions for authors
  • What additional condition makes Proposition 2.4’s nonzero-shift conclusion valid, and does it apply to the trained PFS mapping?
  • What explains the F-ConV zero-perturbation discrepancies and the mixed threshold protocols in Table 5? Do these differences also affect the image lists, preprocessing, or checkpoint selection in Table 1 and Table 7? Please clarify how the main MDMF run was selected among the reported seeds.
3 comments

Sorry, I inadvertently omitted the references corresponding to [A–C] in my review:

[A] Learning Deep Kernels for Non-Parametric Two-Sample Tests. ICML 2020.

[B] Detecting Machine-Generated Texts by Multi-Population Aware Optimization for Maximum Mean Discrepancy. ICLR 2024.

[C] Physics-Driven Spatiotemporal Modeling for AI-Generated Video Detection. NeurIPS 2025.

AuthorsOpenReview ↗

[1/2] Rebuttal by Authors

Thank you for your careful and constructive review. Here are our detailed replies.

W1 (Q1): Condition for a nonzero shift in Proposition 2.4

R1: Thanks for the precise counterexample. We would like to first clarify that the proof in Appendix B.2 keeps the Taylor remainder ϵ\boldsymbol\epsilon and concludes ∣ΔPFS∣2≥ρ2∣Q(μdefect)∣2−∣ϵ∣2\\|\Delta_{\mathrm{PFS}}\\|_2\ge\frac{\rho}{2}\\|\mathcal Q(\boldsymbol\mu_{\mathrm{defect}})\\|_2-\\|\boldsymbol\epsilon\\|_2, but the statement of Proposition 2.4 omits the condition that the quadratic term dominates this remainder. As your example shows, Q(μdefect)≠0\mathcal Q(\boldsymbol\mu_{\mathrm{defect}})\neq\mathbf 0 alone is not sufficient. Following your suggestion, we have corrected Proposition 2.4 and its proof in Appendix B.2 with a condition that controls the remainder.

Theoretically, under Assumption 2.3 with aia_i independent of (ui,si)(\mathbf u_i,s_i) and with the same distribution of ui\mathbf u_i for real and generated images, the shift has the exact form ΔPFS=ρ,D(μdefect)\Delta_{\mathrm{PFS}}=\rho\\,\mathbf D(\boldsymbol\mu_{\mathrm{defect}}) with D(μ):=E[ϕθ(u+sμ)−ϕθ(u)]\mathbf D(\boldsymbol\mu):=\mathbb E[\phi_\theta(\mathbf u+s\boldsymbol\mu)-\phi_\theta(\mathbf u)]. Hence ΔPFS≠0\Delta_{\mathrm{PFS}}\neq\mathbf 0 for every ρ>0\rho>0 if and only if D(μdefect)≠0\mathbf D(\boldsymbol\mu_{\mathrm{defect}})\neq\mathbf 0. If, in addition, ∣∇2ϕθ,ℓ(e)−∇2ϕθ,ℓ(0)∣op≤L3∣e∣2\\|\nabla^2\phi_{\theta,\ell}(\mathbf e)-\nabla^2\phi_{\theta,\ell}(\mathbf 0)\\|_{\mathrm{op}}\le L_3\\|\mathbf e\\|_2 on a convex set that contains every segment from u\mathbf u to u±μ\mathbf u\pm\boldsymbol\mu, the random sign ss cancels the first-order terms, and DℓD_\ell differs from 12μ⊤∇2ϕθ,ℓ(0)μ\frac12\boldsymbol\mu^\top\nabla^2\phi_{\theta,\ell}(\mathbf 0)\boldsymbol\mu by at most L3∣μ∣22(12E∣u∣2+16∣μ∣2)L_3\\|\boldsymbol\mu\\|_2^2(\frac12\mathbb E\\|\mathbf u\\|_2+\frac16\\|\boldsymbol\mu\\|_2). A nonzero shift is therefore guaranteed if, for some output ℓ\ell, ∣μ⊤∇2ϕθ,ℓ(0)μ∣>L3∣μ∣22(E∣u∣2+13∣μ∣2).|\boldsymbol\mu^\top\nabla^2\phi_{\theta,\ell}(\mathbf 0)\boldsymbol\mu|>L_3\\|\boldsymbol\mu\\|_2^2\big(\mathbb E\\|\mathbf u\\|_2+\tfrac13\\|\boldsymbol\mu\\|_2\big). In your example, D=0\mathbf D=0 and the smallest valid L3L_3 on [−1,1][-1,1] is 12, so the condition reads 2>42>4 and correctly excludes this case.

For the trained PFS, the exact form above holds for any bounded ϕθ\phi_\theta, so it applies to the trained head under the same assumptions. We do not claim that the trained head satisfies the sufficient condition. The shift ΔPFS\Delta_{\mathrm{PFS}} is the difference between the mean PFS of generated and real patches, so we measure it directly. On the ImageNet test set, this shift is nonzero for all nine generators under each of the five trained heads with W = 32 in Table 10, and none of the 45 image-level bootstrap 95% confidence intervals contains zero. We have stated both conditions on aia_i and ui\mathbf u_i explicitly in Assumption 2.3 and added the measured shifts to Appendix E.4.

W2: Spatially ordered fields in Eq. 4

R2: Thanks for this careful reading. The kernel in Eq. 4 indeed acts on the PFS field Zθ(x)∈RK\mathbf Z_\theta(x)\in\mathbb R^{K}, i.e., the K=49K=49 patch signatures of an image in their spatial order. Our measurement shows that the score depends only weakly on this order. We re-scored the ImageNet test images using the five trained heads with W = 32 in Table 10 after randomly permuting the 49 positions in the field of every test image, while the reference fields keep their order and no head is retrained. Cells report AUROC / AP (mean±std over the five runs).

Scoring ruleAUROC / AP
Eq. 4 (Table 10)94.97±0.45 / 96.65±0.27
Test positions permuted94.46±0.83 / 96.41±0.44

Random permutation lowers the AUROC by about 0.5 on average, which shows that the detection signal is carried mainly by the values of the patch signatures, while their spatial arrangement plays a minor role. We have revised Section 2.3, the caption of Figure 2 and the hard-voting comparison in Section 3.3 so that they describe Eq. 4 as a Gaussian kernel on the ordered field of the KK patch signatures, and added this analysis to Appendix E.4.

W3: Heatmaps and verified defects

R3: Thanks for pointing this out. The heatmaps are a qualitative visualization (Appendix D.3), and the quantitative evidence for patch-level modeling comes from the comparisons with global pooling on the same frozen backbone (Tables 2 and 7) and from the linear probes of the learned patch representation (Table 8). As you note, the heatmaps do not establish that the final scores localize verified defects. We have revised the caption of Figure 5 and the corresponding text in Section 3.3 and Appendix F to present the heatmaps as qualitative patterns of local responses.

AuthorsOpenReview ↗

[2/2] Rebuttal by Authors

W4: Established components

R4: Thanks for this constructive comment. MDMF does not claim a new MMD estimator or kernel-learning objective, and Section 2.3 builds on the deep-kernel test of [1] and the reference-based scoring of [2, 3]. We would like to reclaim that our work is novel in introducing a patch-level formulation of single-image detection, i.e., comparing the field of patch forensic signatures of one image with the fields of a population of real references. An MMD objective on a global image-level output does not improve over BCE, whereas the MMD objective of MDMF on the PFS field gives the best result (Table 2), which shows that the gain of the MMD objective depends on the PFS field. A generic 128-dimensional deep-kernel featurizer on the same patches reaches 91.87 average AUROC (Table 9), below the five-run average of MDMF (94.97, Table 10). We have revised the contribution statement in Section 1 to credit the deep-kernel test and the reference-based scoring to [1–3] and to state the patch-level formulation above.

[1] Learning Deep Kernels for Non-Parametric Two-Sample Tests. ICML 2020

[2] Detecting Machine-Generated Texts by Multi-Population Aware Optimization for Maximum Mean Discrepancy. ICLR 2024

[3] Physics-Driven Spatiotemporal Modeling for AI-Generated Video Detection. NeurIPS 2025

W5 (Q2): Threshold protocols in Table 5

R5: Thanks for spotting this. All baseline rows of Table 5 are imported from the GenImage table of [5], which collects results reported under different protocols. Some rows, such as the CNNspot accuracy of 39.8 on GLIDE that you noted, come from [4] with a fixed decision threshold, while [5] selects the threshold of F-ConV per evaluation, as we do for MDMF (Appendix D.2). We have stated the source and threshold protocol of the rows in the caption of Table 5 and limited the accuracy comparison in Appendix E.1 to F-ConV. Under the same per-evaluation threshold, MDMF obtains a higher average ACC than F-ConV (91.0 vs. 90.1), and Table 1 compares all methods by the threshold-free AUROC and AP.

[4] GenImage: A Million-Scale Benchmark for Detecting AI-Generated Image. NeurIPS 2023

[5] Detecting Generated Images by Fitting Natural Image Distributions. NeurIPS 2025

W6 (Q2): F-ConV at zero perturbation, and Tables 1 and 7

R6: Thank you for this careful cross-check. The difference comes from the F-ConV model that we retrained and evaluated for the robustness study, and Table 1 and Table 7 are not affected.

F-ConV in Tables 14 and 15. The F-ConV row of Table 1 is the five-seed average reported in [5] on the same benchmark. For Tables 14 and 15, we retrained one F-ConV model with its official code and evaluated it with our perturbation script on 1,000 real and 1,000 generated images sampled per generator and severity level, with the randomized test-time transformations of F-ConV. The 91.25 and 91.00 you mentioned are the results of this single model on two separately drawn samples of images. Within Tables 14 and 15, every severity level of F-ConV is evaluated with the same model and pipeline, so the degradation of F-ConV is measured consistently. MDMF is evaluated on the full test sets throughout, so its values at zero blur and zero noise equal those of Table 1.

Table 1 and Table 7. MDMF, the baselines that we reproduced and all variants of Table 7 are evaluated on the same full test sets of the nine ImageNet generators, and the remaining baseline rows of Table 1 are taken from [5], which uses the same benchmark. MDMF and all variants of Table 7 share the same frozen DINOv2 ViT-L/14 backbone and preprocessing, and each checkpoint is selected by AUROC on the ProGAN validation split, which contains no test generator. We have revised Appendix E.8 to state the evaluation protocol of each method in the robustness study, stated the checkpoint selection in Appendix D.3, and marked the rows of Table 1 that are taken from [5].

W7 (Q2): Selection of the main MDMF run

R7: Thanks for this question. The 95.65 AUROC of Tables 1 and 7 that you mentioned is the result of our first training run, which uses seed 0 (Seed = 0 in Table 12). We did not select it among the reported seeds, and the other four seeds were trained after this run. The checkpoint of this run is selected by AUROC on the ProGAN validation split without access to test data. Across the five runs, MDMF obtains 94.97±0.45 AUROC and 96.65±0.27 AP, which remain above the five-seed average of F-ConV reported in [5] and Table 1 (93.77 AUROC and 93.38 AP). We have marked the MDMF row of Table 1 as the seed-0 run and added the five-run mean and standard deviation to the caption.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response

We sincerely thank the Area Chair and all reviewers for their time and constructive feedback. We are glad that the reviewers find the problem well motivated, in that detection should attend to local micro-defects instead of relying only on global semantic cues (zQPh, xMM7), and the theoretical analysis beneficial (xMM7). We also appreciate that the reviewers find the evaluation broad across four benchmarks and many baselines (tNP3, zQPh), including the experiments on generated videos (xMM7), the method robust to the choice of encoder and to post-processing (zQPh), the empirical gain meaningful on the same frozen backbone (tNP3), and the paper well-organized and easy to follow (xMM7).

We have responded to every comment point by point in the individual responses, supported by new experiments and analyses. All revisions are marked in red in the revised PDF, and we summarize the main ones below.

Patch-level formulation and evidence for local modeling (tNP3, zQPh, xMM7)

  • Compare MDMF with previous local-artifact detectors and deep-kernel MMD methods, and state the patch-level formulation in the contributions (see Section 1 and Table 18 in Appendix C)
  • Evaluate MDMF and the global-pooling baseline on real photos with one inpainted region (see Table 25 in Appendix E.12)
  • Analyze the dependence of the detector score on the image class and on the order of the patch signatures (see Tables 20 and 21 in Appendix E.4)

Theoretical analysis (tNP3, xMM7)

  • Refine Proposition 2.4 with a condition that controls the Taylor remainder, and clarify the scope of Theorem 2.7 (see Section 2.4 and Appendix B.2)
  • Extend the analysis to a general defect model and report the measured PFS mean shifts (see Proposition B.6 and Table 22 in Appendix E.4)

Recent generators and stronger baselines (zQPh, xMM7)

  • Evaluate MDMF, AIDE and Effort on X-AIGD with 13 recent text-to-image generators (see Table 19 in Appendix E.1)
  • Compare with AIDE and Effort on OpenSora and under post-processing perturbations (see Figure 3 and Table 24 in Appendix E.8)

Reference set and evaluation protocol (tNP3, xMM7)

  • Analyze the composition of the reference set, including cross-domain references (see Table 23 in Appendix E.7)
  • Detail the evaluation protocols of the baselines and the robustness study (see Appendices D.3, E.1 and E.8)

We hope that these revisions address the reviewers' concerns, and we would be happy to clarify any further questions during the discussion period.

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

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