Detectors that flag AI-generated images work well on the generator they were trained on and often fall to near chance on new ones. The usual explanation is that they learn fingerprints specific to one generator. This note proposes a different, testable explanation for detectors built on large frozen image models such as CLIP. Their "fake" decision may be tangled up with a simpler cue: how far an image looks from an ordinary photograph. Generators differ a great deal in how painterly, smooth or stylized their outputs look. A detector that partly keys on "looks non-photographic" will therefore generalize well to some generators and poorly to others, for reasons that have nothing to do with how the pixels were actually made.
To test this we borrow a measuring tool from style transfer research. Style transfer (repainting a photo in an artistic style) has a known trade-off curve between how strongly the style is applied and how well the original scene's structure survives. Improving Style Transfer with Calibrated Metrics fits two human-calibrated scores to this curve, style effectiveness $E$ and content coherence $C$. The plan is to move real photographs and generated images along that curve together, holding their "look" matched, and measure whether a detector's score follows provenance or follows $E$. From the result we derive a cheap score that can be computed before deployment. It asks whether a frozen backbone can separate provenance from style at all, and we test whether that score predicts cross-generator failure.
Core Claim
For detectors built on frozen or lightly adapted foundation models, part of the cross-generator gap is a style shortcut. The linear direction that separates real from fake in feature space is correlated with the direction along which style effectiveness $E$ increases. The claim has three consequences, all testable. First, real photographs pushed along the frontier by non-generative stylization will be flagged as fake more often as $E$ grows. Second, when real-derived and generated images are matched in $(E, C)$, frozen features will separate them much worse than on standard benchmarks. That matched-pair separability is our a priori measure of representation rigidity, meaning the ceiling imposed when the backbone's frozen features lack the needed distinction. Third, across detector variants, the amount of style leakage will predict accuracy on unseen generators on GenImage and Chameleon.
This is not the same as evaluating detectors on stylized images. Breaking Latent Prior Bias already built a Style Diversity split of 183 styles into GenImage++. That split treats style as a categorical nuisance and contains only generated images, so it cannot separate "generated" from "stylized." Our contribution is the controlled, continuous, provenance-crossed design and the predictive rigidity score derived from it.
Why these three directions meet here
The rigidity literature motivates the second consequence. In pathology, prompt-based MRI adaptation and nighttime tracking, lightweight adapters cannot create features the frozen backbone never learned (Lai et al., Feng et al., DCPT). That literature also lacks a diagnostic that can be computed in advance; it detects rigidity only after performance collapses. The forensics literature shows the same pattern in a different vocabulary. FatFormer argues that frozen CLIP misses forgery traces and adds wavelet adapters. Effort shows that naive fine-tuning collapses the feature space to one or two dominant directions, and it trains only an orthogonal residual subspace. Neither paper asks what those one or two directions encode.
Our hypothesis is that one of them is "non-photographic look." Yeh et al. supply both the instrument and a warning. The identity of the style image explains more output variance than algorithm settings, so any probe must sample many styles and model style identity as a random effect. K-LoRA supplies a generation-side tool. Its schedule applies content early in denoising and style late, which lets us produce generated images whose position on the frontier we can control.
Research Program
The first component is a Frontier Probe dataset. It starts from a pool of real content photographs, drawn from the real halves of GenImage and COCO, and a pool of several hundred style images from WikiArt. We make three versions of each content–style pair. The first is real-derived: the photo is stylized with non-generative methods (Gatys-style optimization, and AdaIN, which swaps feature mean and variance statistics) at a sweep of style weights. The second is generated: a diffusion model rewrites the same photo with a style LoRA at a sweep of strengths, on SDXL and FLUX.1, using K-LoRA-style scheduling. The third is a generated control with no style, a plain diffusion reconstruction of the photo.
We compute $E$ and $C$ for every image with the Yeh et al. procedure and bin images on the $(E, C)$ plane. Within each bin we then have real-derived and generated images with matched look. We also include ProPIH composites, where real COCO objects are harmonized into paintings, as a localized-stylization stress case.
One labeling choice must be stated plainly. Classical style transfer also synthesizes pixels, so "real" here means "not produced by a generative model's decoder." That is the property deployed detectors are asked to flag. We report results under both labelings so that readers who disagree can still use the data.
The second component is two quantities computed on this probe. The first is style leakage $\lambda$, the share of variance in a detector's logit on real-derived images that is explained by $E$. We estimate it with a mixed model that has a random effect for style identity. The second is matched separability $\rho$, the AUC of a linear probe trained on frozen features to separate real-derived from generated images within matched $(E, C)$ bins, evaluated on held-out styles. A low $\rho$ with a high standard-benchmark AUC means the backbone's easy real/fake signal is mostly look. A low $\rho$ that stays low under adaptation means the backbone lacks a provenance feature at matched style, which is rigidity in the precise sense.
The third component is two causal interventions that test whether the shortcut matters for cross-generator accuracy. In the first, we estimate a low-dimensional style subspace by regressing frozen features of real-derived images on $E$, then project it out before the detector head. In the second, we retrain with frontier-swept real-derived images labeled real. If the shortcut is causal, both interventions should improve accuracy on unseen generators whose outputs sit far from the training generator's position on the frontier, and should help little on generators near it.
Baselines
The naive reference is the frozen CLIP ViT-L/14 penultimate-layer linear SVM of Raising the Bar of AI-generated Image Detection with CLIP. It reports a +6% average AUC gain on unseen generators over prior detectors, but the file gives no absolute value. It is the purest "frozen backbone" condition, so it should show the most leakage. We retrain it on the same training generator used for every other method, SDv1.4 from GenImage.
The strongest existing method on these benchmarks is OMAT from Breaking Latent Prior Bias: CLIP with rank-4 LoRA, trained on adversarial examples found by searching the diffusion model's starting noise. It reports 94.63% average accuracy across GenImage subsets against 79.20% for plain CLIP+LoRA, 96.78% on GenImage++, and 66.05% on Chameleon against AIDE's 62.60%. Because OMAT costs roughly 79 GB of VRAM per example, we will use released checkpoints if available. Otherwise we run OMAT on a reduced example budget and report the budget explicitly.
We also include Effort, which reports an average AUC of 0.940 over deepfake and generator benchmarks. It is the method most directly about which directions the detector uses. We further include FatFormer, which reports 95.0% on unseen diffusion models versus UniFD's 85.4%, and SAFE, which reports a +4.5% accuracy gain over prior methods across 26 generators; the file gives no absolute number for SAFE. These three span wavelet-based, crop-based and subspace-constrained designs.
For fairness, every retrained method uses the same SDv1.4 training split and the same image preprocessing. Each gets an equal hyperparameter search of 20 trials selected on a held-out generator that is never used for testing. No method sees Frontier Probe images, except in the augmentation intervention, where the same images are made available to every method that is retrained with it.
The key ablation separates style removal from simply removing some feature capacity. We project out a random subspace of the same dimension, and separately a subspace fit to $C$ instead of $E$. The proposal is supported only if removing the $E$-subspace improves cross-generator accuracy and these controls do not.
There is no reported result on Lacuna for any detector's false-positive rate as a function of calibrated style effectiveness, nor for matched-look separability. Those numbers are what this work produces. Beating the baselines means that projection or frontier augmentation lifts the worst unseen-generator accuracy on GenImage and Chameleon beyond seed variance, and that it does so without lowering GenImage++ accuracy.
Why not just…?
Why not just evaluate on the GenImage++ Style Diversity split? It contains only generated images, so a detector that flags "stylized" and a detector that flags "generated" get identical scores on it. Its styles are categories, not positions on a calibrated trade-off curve. It can show that stylized fakes are hard. It cannot show why, and it cannot measure leakage.
Why not just add stylized real images to training as extra "real" examples? This is a real threat to any claim that a new training method is needed, which is why we do not propose one. Frontier augmentation is one of our two interventions. If it closes the gap as well as projection does, that still confirms the shortcut hypothesis, and it becomes the recommended fix. What augmentation cannot provide is the diagnostic. $\lambda$ and $\rho$ are computed without retraining, and they tell a practitioner whether a given backbone is style-contaminated before any augmentation is chosen.
Why not just use a higher-rank adapter or full fine-tuning to escape rigidity? ABBA-Adapters shows that higher-rank updates beat LoRA on language tasks, which suggests that capacity could raise $\rho$. Effort, however, shows that more freedom during forensic training can collapse the features onto a few shortcut directions. Extra capacity may therefore amplify the style cue rather than remove it. We test this directly by measuring $\rho$ and $\lambda$ for LoRA at ranks 4 and 16 on the CLIP backbone and for full fine-tuning. The capacity explanation predicts that $\rho$ rises with rank. The shortcut explanation predicts that $\lambda$ rises with rank.
Why not just rely on OMAT's noise-seed fix? OMAT removes a shortcut tied to the diffusion model's starting noise. Style, by contrast, is applied late in denoising, as K-LoRA's schedule illustrates, so it may survive OMAT training untouched. Running OMAT through the Frontier Probe settles this. If its $\lambda$ is near zero, the style shortcut is already handled, and our contribution narrows to the diagnostic.
Proposed Experiments and Decisive Checks
The first check is the flip curve. We plot the fake-probability each detector assigns to real-derived images against $E$, across many styles. A monotone rise that survives the style random effect supports the first consequence. A flat curve refutes the hypothesis for that detector.
The second check is matched separability. We compare $\rho$ against each backbone's standard GenImage AUC for frozen CLIP, frozen DINOv2 as used by WaRPAD, and their adapted versions. A large gap between the two numbers is the rigidity signature.
The third and decisive check is prediction. Across roughly fifteen detector variants (backbones, layers, adapter ranks, and the published methods above), we rank-correlate $\lambda$ on the probe with accuracy on each unseen GenImage generator and on Chameleon, and we report bootstrap confidence intervals. We are candid that fifteen points gives limited statistical power. For that reason, the per-generator analysis must also hold: detectors should lose the most accuracy on generators whose outputs have a mean $E$ farthest from the training generator's.
The fourth check is the causal intervention described above, together with its random-subspace and $C$-subspace controls.
As a robustness check, the $C$ metric agrees with humans only about 69% of the time. We therefore repeat the binning with DINO feature similarity as an alternative measure of content preservation, and treat any conclusion that flips as fragile.
References
- Improving Style Transfer with Calibrated Metrics
- Breaking Latent Prior Bias in Detectors for Generalizable AIGC Image Detection
- Bridging the Pathology Domain Gap: Efficiently Adapting CLIP for Pathology Image Analysis with Limited Labeled Data
- Learning Federated Visual Prompt in Null Space for MRI Reconstruction
- DCPT: Darkness Clue-Prompted Tracking in Nighttime UAVs
- Forgery-aware Adaptive Transformer for Generalizable Synthetic Image Detection
- Orthogonal Subspace Decomposition for Generalizable AI-Generated Image Detection
- K-LoRA: Unlocking Training-Free Fusion of Any Subject and Style LoRAs
- Progressive Painterly Image Harmonization from Low-Level Styles to High-Level Styles
- Raising the Bar of AI-generated Image Detection with CLIP
- Improving Synthetic Image Detection Towards Generalization: An Image Transformation Perspective
- ABBA-Adapters: Efficient and Expressive Fine-Tuning of Foundation Models
- Training-free Detection of AI-generated images via Cropping Robustness