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- Confidence
- 4
- Informativeness
- 2
- Presentation
- 1
- Soundness
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Paper summary
The paper suggests that existing detectors are evaluated in settings where the real images are common everyday natural images. This overlooks a critical set of real images, ones that do not look generic, but are not AI-generated. The paper curates a benchmark of 795 such images and tests this very hypothesis. With a control group of natural looking real images, the authors measure the elevation in false positive rate (real classified as fake) to get a sense of this. The major takeaways are (i) Most detectors conflate implausible looking images with fake images, (ii) Artifacts in post-processing also happen to contribute to this. (iii) There are not a lot of images that are commonly misclassified by detectors (iv) This issue is simple to overcome via training. The authors also conduct other experiments to study spectral properties, impact of "salient" regions of the image etc.
Critical strengths
- The overall research question and finding is interesting. It is also one of practical importance, especially in domains such as art where there are real images which do not look like everyday scenes.
- The main experiment is rigorous with sufficient controls such as a reference COCO set (also with Matching), adding to the validity of the findings.
Critical weaknesses
- The paper writing could be improved I feel. I find the message very interesting, but the writing style made it extremely difficult for me to follow here. I will add specifics below, a) Abstract has too much information which makes it hard for the first time reader: for instance the control checks (which reduce 10 to 7 is something done for empirical rigor, which is good, but also served confusing for me to grasp that early on into the paper, also the control benchmark sanity was not clear to me so early on into the paper, the takeaway should have just been mentioned as multiple detectors falsely classify such real images as fake. I would suggest avoiding so many readings in the abstract in general, especially given that the paper is not about those particular numbers, but the broader trend). b) I felt elevation was a somewhat unnatural word to use in lines 22 and 88 (although it made sense after reading the intro) c) Line 155: What does interpretable mean here? To me it feels like the role of the control is to ensure that the detector is a reliable one (since it is not informative to test a poor quality detector) d) Section 4.4 directly starts with results, I feel it would be better to start with 1 or 2 sentences motivating what the experiment is trying to do and why these metrics are the right fit.
- The paper studies a nice topic, but I would like it if it would provide more predictive power. For instance, it suggests that there is no common type of abnormal real image where all detectors fail (sec 4.4). It also seems to not actually use information from the training data, algorithm, architecture, initialization etc to link the way in which these models fail to provide further insights. The paper in its abstract talks about detectors ranging from 6 families, but the regularities within those families are not used in the analysis. Natural questions that arise (i) what makes Haywoodsloan special here, (ii) why do CLIPDet (Cozzolino et al) and UFD (Ojha et al) behave differently when they have roughly similar training recipes.
- Section 4.9: It would be helpful if the authors can clarify how this is a true test of generalization, for instance, the 396 training images in this case might have significant overlap with the test images.
Questions for authors
- [1] argues that a major issue with fake-image detectors is their tendency to learn features associated with the real-image distribution, even though these associations are almost-always spurious. For instance, a detector trained on relatively low-quality GAN images might learn to associate high image quality with real images. Such associations can also indirectly influence what the detector treats as evidence for fake images: if natural scenes are strongly associated with real images, their absence might contribute to a fake prediction. I wonder whether the authors see a connection between this observation and the failures reported on FLORIDA. The authors also release a Corvi +, which claims to have less reliance of real features, it would be helpful to see what happens if this model is evaluated on the FLORIDA dataset.
- Sec 4.3 suggests that for Corvi, the entire discrepancy is an artifact of post-processing. Which intuitively makes sense, since Corvi is trained on 96x96 crops of the images, implying that it is less likely to pick up on global, semantic abnormalities, I would like to know the authors thoughts on this, as well as analysis of similar methods and their failure modes.
- Linked to above, but the paper seems to suggest that the simple way of overcoming this issue is with additional training data, but this assumes a certain awareness of the kind of images seen at test time. It would be nice to have ways to build generalizable detectors which do not assume knowledge of the training distribution (for instance Corvi and Haywoodsloan) seem to achieve robustness. I would be glad to know the authors thoughts on this regard.
I really like the core idea behind this work personally, and I think adding some predictive value behind these observations would make me view the work in a much more positive light.
References
- 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 comments
part II
Comment 3 of 4 — Section 4.9: is it a true test of generalization?
You are right that training and test images from one collection can overlap, and the paper did not address it enough. We now report the following checks, and keep one caveat.
- Similarity audit. For the CLIP probe we computed each test image's maximum cosine similarity to the 396 training images and evaluated only the least-similar half and quartile. FPR falls from 46% / 44% (no hard negatives) to 1.5% / 3.0% (w = 4).
- Source-batch hold-out. FLORIDA ships as four collection parts (PART1–4). We held one out entirely, trained with 396 hard negatives from the other three, and tested only on the held-out part. At w = 4, CLIP falls from 44–69% to 1.7–3.0% FPR on each held-out part; Corvi from 10–42% to 0.4–13.4%.
- Category hold-out (already in the paper): leaving a whole taxonomy category out of training still collapses its FPR.
- Control for generic real data. Adding the same number of provenance-matched or unmodified ordinary COCO images leaves CLIP's FPR at 41–59%, so the effect is specific to FLORIDA's images, not simply more real supervision.
Caveat. The parts are collection batches, not guaranteed to be source-disjoint, and all of these tests stay within one collection. An independently sourced test set is the clean answer, and we say so in Limitations.
Comment 4 of 4 — Questions 1–3
Q1: Stay-Positive and Corvi⁺. We see a plausible connection. Stay-Positive argues that detectors learn spurious real-image features, so the absence of such features can push a prediction toward "fake". Our spectral analysis found FLORIDA images carry less high-frequency power than ordinary photographs and even than generated images, and AEROBLADE's evidence concentrates in smooth, low-salience regions, which fits that picture. But we cannot test it directly: we could not locate released Corvi⁺ weights or code. As a weak substitute we tried the idea on our own probe (non-negative last layer on Corvi's frozen features, our training data). It did not reduce FLORIDA false positives (40.0% vs 25.6%) and 99.5% of its weights went to zero, so we regard it as inconclusive and not as evidence about their model.
Q2: Corvi and post-processing. We agree, and have supporting evidence. Corvi flags 26.0% of JPEG FLORIDA images but only 1.1% of WebP ones; processing covariates alone predict its failures (AUROC 0.76) while atypicality does not (0.47); and a processing-stress envelope reproduces and exceeds its FLORIDA false-positive rate on ordinary photographs (38% vs 26%). This is consistent with a detector keyed to local compression traces more than to scene content. We have not independently verified the training-crop size you mention, so we do not rely on it: our argument rests only on the measurements above. We run Corvi at full resolution, as in the authors' released configuration. Corvi is not robust in practice, since its FPR is 10× its control rate; the its FPR is 10× its control rate, and our evidence points to processing history rather than scene content, though we cannot rule out a small residual
Q3: Generalizable detectors without knowing the test distribution. We agree that a data fix presupposes awareness of the tail. Two observations bear on how much awareness is needed: hard negatives from other taxonomy categories and from other collection batches still transfer to held-out ones, so the specific kind of fake-looking image need not be known in advance, but some sample of the tail is needed. Corvi is not a counterexample to this (above), and Haywoodsloan is the only detector that is robust, for reasons we cannot establish. Constructing detectors that need no such knowledge is, we agree, the more important goal; our contribution is a benchmark and protocol that can tell whether a candidate achieves it.
Reviewer Response
I thank the authors for taking the time to provide a rebuttal and fix the writing issues.
Predictability: The recent experiments establish the influence of some factors (post-processing, atypicality etc), however I still feel the paper lacks a general theme behind this phenomenon (when does a detector fail on unnatural real images vs when does it not). The Haywoodsloan not providing documentation is a valid concern, however it does not offer the reader a lot of understanding about the topic as a result. I also believe achieving a more predictive understanding of this would result in a solution which is more generalizable than "training on parts of the FLORIDA dataset".
True Test of Generalization: I feel more confident regarding the generalization, but the doubt still remains as to why any exposure to the FLORIDA dataset is needed for generalization.
As a result, I will be keeping my score.
part I
Comment 1 of 4 — Overview and presentation
Thank you for a thoughtful review and for liking the core idea. You raise two things: the writing, and predictive power. We have acted on both; the second is partly achievable, and we say where it is not.
Writing (all four points fixed in the revised PDF). (a) The abstract is rewritten: no control-gating details and far fewer numbers; it now says that most detectors flag many more real photographs as AI-generated than ordinary photographs (up to 80% for one detector), and gives the broader trend. (b) "Elevation" is replaced throughout by plain wording ("higher false-positive rate", "increase"). (c) You are right about the role of the control. It is there to show that a detector is reliable on ordinary photographs, so that failing on FLORIDA is informative. The Introduction and Section 3 now say "reliable" and no longer use "interpretable". (d) Section 4.4 now opens with why the experiment matters (if every detector failed on the same images, one shared cue would explain it and ensembling could not help; otherwise each detector's own training matters) and why we use two metrics (pairwise overlap is easy to read but weak for joint dependence among seven detectors; the vote-count distribution uses all seven).
On Section 4.4's conclusion itself: following another reviewer's request we compared the full vote-count distribution with an independent-error baseline. It is over-dispersed (variance 1.87 vs 1.30 expected, p < 10⁻⁴), so detectors fail on largely different images but not independently; we withdrew the claim of independence.
Comment 2 of 4 — Predictive power: Haywoodsloan, CLIPDet vs UnivFD, and families
We agree the paper did not use what is known about training or architecture to explain failures. We ran two controlled analyses. They give partial answers, and we report where they do not.
CLIPDet vs UnivFD (same recipe, different behavior). The two heads differ in backbone weights (CommonPool vs OpenAI CLIP ViT-L/14), preprocessing (CLIPDet resizes the whole image to 224 px; UnivFD takes a 224 px center crop of the native-resolution image), and training data. We trained probes with identical data, split and calibration on each backbone × preprocessing combination, without hard negatives, and measured the share of held-out FLORIDA images flagged:
For reference the released heads flag 81.2% and 42.4% of the same images. So backbone and preprocessing do not explain the roughly 2× gap between the released heads; in our probes this points to training data or objective (to our understanding, UnivFD's head is trained on GAN fakes and CLIPDet's on latent-diffusion data). We could not vary training data here, so that remains a hypothesis.
Which images fail. We predicted each released detector's per-image error from processing covariates (area, JPEG quality, WebP flag), atypicality (distance to ordinary photographs in a neutral DINOv2 embedding) and taxonomy category (5-fold CV AUROC; 0.5 = chance):
Predictability is partial and detector-specific: Corvi's failures follow processing (below), CLIPDet's depend on both processing and atypicality, and AEROBLADE's are not predicted by any of these. We do not claim a general predictive theory.
Haywoodsloan. We cannot say what makes it robust. Its model card documents no training data (an AutoTrain fine-tune of its own earlier version), so we cannot exclude exposure to images like ours; it is immune to our processing manipulations; and its errors (4.9%) are too few to model. We state this limitation in the paper rather than offer an explanation we cannot test.