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Withdrawn from ICLR 2027

ReSCOPE: Learning Reconstruction-Consistent Representations for Generalizable AI-Generated Image Detection

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Detectors trained on a single generator often rely on generator-specific cues that transfer poorly to unseen generators. We use consecutive reconstruction to investigate whether label-preserving reconstruction variations can provide a training signal for improving cross-generator generalization. Since consecutive reconstructions share the same fake label, their feature discrepancy reflects the encoder's sensitivity to an additional reconstruction rather than a change in real/fake labels. We use this signal to reduce reconstruction sensitivity while preserving real/fake discrimination, encouraging the encoder to learn more stable forensic cues that transfer across generators. We propose ReSCOPE, a reconstruction-consistent adaptation framework that aligns encoder representations of consecutive fake–fake reconstruction pairs while retaining source-domain real/fake supervision. Training alternates between (i) joint optimization of source-domain classification and reconstruction consistency and (ii) consistency-only adaptation. In the adapted representations, distances between consecutive reconstructions decrease while classification margins for images from unseen generators increase. Reconstruction is used only for offline training-pair construction and is not required at inference. With single-generator training, ReSCOPE achieves 97.57% mean accuracy on GenImage and 88.93% overall accuracy on Chameleon. It also improves generalization on additional curated and in-the-wild benchmarks.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
AI-generated image detection, cross-generator generalization, diffusion reconstruction, representation learning

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_A9bQOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

The paper studies AI-generated image detection with one training generator and unseen test generators. Its method, ReSCOPE, reconstructs each real image twice with the frozen diffusion model SD1.4 (DDIM inversion, then denoising), giving a pair of fakes. It fine-tunes CLIP ViT-L/14 or SigLIP2-Giant with rank-4 LoRA on GenImage SD1.4, using BCE plus a cosine consistency loss that pulls the pair's normalized features together. Training alternates phases with both losses and phases with the consistency loss alone. An analysis reports that the pair's feature difference lies in local low-dimensional subspaces. The paper claims 97.57% mean accuracy over generators (mAcc) on GenImage and 88.93% accuracy on Chameleon. It tests the SigLIP2 detector on six more benchmarks against baseline numbers taken from prior papers. An ablation on both backbones compares it with BCE-only training and a linear classifier on frozen features (the linear baseline).

Critical strengths

On the same backbone, the alternating consistency schedule beats BCE-only training, and inference needs no reconstruction.

In Table 7, with CLIP, mAcc rises from 80.09% for BCE-only training to 93.37% for ReSCOPE. With SigLIP2, it rises from 89.75% to 97.57%. This is the only matched comparison in the paper. But each setting is a single run, and the controls start from a different initialization (App. B.4). So I read it as suggestive evidence only.

Critical weaknesses
  1. The method recombines known studies, and the paper never shows why aligning two reconstructions should remove generator-specific cues.

    • The training data, the pair and the loss each appear in earlier work. DRCT (Chen et. al., ICML 2024) and PPL (Yang et. al., ICLR 2026) already train on diffusion reconstructions of real images and align features within a label. PPL, the strongest baseline in Table 1, does this with LoRA on CLIP under the same GenImage SD1.4 protocol. DID (CVPR 2026) already uses the same pair of consecutive reconstructions (l.108–109). The loss is that of CORE (Ni et al., CVPR Workshops 2022), which the paper does not cite: classification plus a cosine consistency without negatives on two same-label views. What is new is the choice of this pair for the alignment, and the schedule.
    • The paper has no rigorous justification for why the method works. The link between the pair's feature difference and generator-specific cues is only a drawing: "The schematic places this response along the axis of source-related variation" (l.202). Both reconstructions carry SD1.4 traces, and nothing explains why invariance to a second pass would remove the signature of the first. The evidence is Fig. 2(c–f): one CLIP detector, one unseen generator (BigGAN) and 500 images.
    • The subspace analysis does not lead to the method. It is contribution 1 (Section 3), but predicting the feature difference and removing its subspace both fail (App. A.2–A.3).
  2. The results do not separate the method from the backbone, the extra data and the protocol, and report no variance.

    • The state-of-the-art claim holds only with a backbone that no baseline uses. The headline result and all cross-dataset tables (2–6) use SigLIP2-Giant at 384 px. The linear baseline alone scores 7.68 points higher with SigLIP2 than with CLIP (Table 7). With CLIP ViT-L/14, ReSCOPE scores 93.37% mAcc, below five baselines in Table 1, including PPL (97.20%). OMAT, a baseline that also fine-tunes CLIP with rank-4 LoRA on SD1.4, scores 94.63%.
    • Extra training data, mismatched protocols and fixed-threshold metrics weaken the comparisons. ReSCOPE also trains on 10K reconstruction pairs, half of them from a pool the paper never describes (App. B.1). The Table 4 baselines are trained on ProGAN, and only ReSCOPE's inputs are re-encoded as JPEG at quality 80 (l.1117–1121). For GenImage, mAcc is the standard metric. Elsewhere, every result is accuracy at a fixed 0.5 threshold. EvalGEN contains only fakes, so a detector that always answers "fake" scores 100%. Accuracy on real photographs (RAISE) drops to 78.40% (l.1138).
    • The margins come from single runs, with a checkpoint chosen on test data. The margin over PPL is 0.37 points, with no standard deviation. The reported checkpoint is the best of six, scored on a subset of the GenImage split used for testing (App. C, Table 13). The six span 0.265 points. Table 7 has no control that adds the reconstructions as extra BCE fakes or uses generic augmentation pairs. So its gain cannot be attributed to the reconstruction pair.
Questions for authors
  1. Please report ReSCOPE (CLIP), the SigLIP2 linear baseline and BCE-only SigLIP2 on Tables 2–6. If ReSCOPE (CLIP) matches the CLIP-based baselines, or if the margin over BCE-only SigLIP2 holds everywhere, that would mostly address this concern.

  2. Please run ReSCOPE, BCE-only training and the variant without consistency-only phases with multiple seeds from a shared initialization and avoid p-hacking by choosing the checkpoints on data disjoint from the GenImage test split.

  3. Which model produced the second reconstruction pool (l.899)? A generator other than SD1.4 would break the single-generator claim. Also, does the SigLIP2 configuration put a fake-classification loss on the pairs (l.929–930)?

  4. If possible, please add two experiments: the reconstructions as extra BCE fakes without the consistency loss, and the consistency loss on pairs of JPEG or blurred views to verify the efficacy of reconstruction pair.

  5. Please report more metrics (such as AUROC, AP, TPR at 1% FPR, and accuracy on real and fake images) on every benchmark. I would like to see if ranking holds without a fixed threshold.

  6. Which variant, resolution and schedule does the SigLIP2 linear baseline use, and was it tuned? It scores 85.24% (Table 7), while other works report 92.0% (2509.12995) and 94.5% (2602.01738) under the same protocol. The claimed 12.33-point gain over it (l.073–075) rests on this number, thus needs better clarification.

Reviewer_pkreOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

Detectors trained on one generator lean on generator-specific cues. The authors probe this by applying a frozen SD1.4 operator twice to a real image. A1 and A2 share the fake label, so their feature discrepancy measures reconstruction sensitivity at fixed label. On 160K triplets the response is locally low-dimensional yet unpredictable, and projecting it out gives no consistent gain. ReSCOPE aligns normalized A1/A2 features with a cosine loss using no negatives, alongside source BCE, alternating Joint and RC-only LoRA phases, and inference needs no reconstruction. One SigLIP2 checkpoint is evaluated unchanged on GenImage and seven further benchmarks, reaching 97.57% mAcc.

Critical strengths

The diagnostic holds up, including what undercuts it. Local structure is measured soundly (22 valid configurations, matched controls, bootstrap CIs), yet prediction fails and hard removal costs 3.4 BAcc in A.3's separate classifiers; negative knowledge, not merely a new loss. The gain is in transfer, not source fitting: ReSCOPE trails DIRE, AIDE and EFFORT on its own training generator (98.18) yet holds the best mAcc and exceeds 95% on all seven unseen generators.

Critical weaknesses
  1. The mechanism is not separated from cheaper explanations. B.1 makes T deterministic, so A2 is just a re-application to A1 and likely a near-duplicate, never quantified in pixels and with no fixed-point check. Nothing excludes (a) a near-duplicate consistency prior: weak augmentation, JPEG, a mean teacher target; the difference from DRCT's same-label contrastive objective stays prose and Table 7 lists no such arm; (b) extra SD-family exposure, since T is SD1.4 and no other operator is tried; (c) collapse, since a loss with no negatives bypassing the head is minimized by a merged fake cluster, while Fig. 2(e)'s 42-fold contraction tracks only pair distance, not spread within the fake class or its effective rank. Joint-only is matched in steps and data yet trails by 6.86/4.80, so alternation is shown at λ = 0.1 only; the missing sweep is a strengthening request, not a confound.

  2. Reproducibility falls short of what is offered as a contribution. B.1 has RC training use "10K pairs, sampled as 5K pairs from each of two reconstruction pools", but defines only the 160K SD1.4 one: the second carries half the supervision, is described nowhere, so it cannot be leakage-checked against the GenImage validation split Table 1 tests on. The ~320K set is a listed contribution, with no release statement, no Limitations, and no GPU model or runtime. Seeds are fixed and no run is repeated, so Tables 1–8 carry no error bars, and the top of Table 1 stays unresolved: 97.57 against PPL's 97.20.

Questions for authors
  1. Would a non-reconstruction near-duplicate arm, same λ, same steps, same starting weights as ReSCOPE, pairs from two weak augmentations or a JPEG round trip, recover the 6.86/4.80 Table 7 gap?
  2. Define the second reconstruction pool behind 5K of the 10K training pairs and say whether its images touch an evaluation split you report.
  3. Does exceeding 95% on the seven unseen generators survive a non-SD reconstruction operator?
  4. Variance within the fake class after adaptation, and effective rank, both backbones against BCE-only? Neither margins nor pair distance exclude collapse behind Fig. 2(e).
Reviewer_mtasOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper proposes a modification to the typical training objectives used to train fake image detectors. The authors take motivation from the idea of image reconstructions – how the reconstructions of real and fake images are different. In this paper, they extend this to include a second round of reconstruction, i.e., reconstructing an already reconstructed real/fake image. They convert the first and second level reconstructions into a feature representations, and obtain their difference, and propose an objective function which constrains this difference to be small for fake images. Using this objective function in conjunction with the typical binary cross entropy loss, the authors show some improvements in fake image detection ability compared to some baselines on some datasets.

Critical strengths
  • Natural images and those created by generative models are different in some fundamental ways. So, it makes sense to do multiple rounds of image reconstructions and see if differences emerge (between real and fake) at later rounds. The authors have proposed going beyond one round of reconstruction, which, I think, could be a useful idea for the community.

  • Some of the results (e.g., Table 2 and 3) show a clear improvement over some of the baselines. Although, please see the weaknesses to understand some caveats.

  • The method is surprisingly robust to different image corruptions (Table 8).

Critical weaknesses
  • The paper is very poorly written. Section 3.1 and 3.2 are not readable, as it is introducing terms and ideas that have not been defined. I am listing just a couple of examples, but by no means this is an exhaustive list.

    • Lines 148 - 150 do not make much sense. No explanation has been given for what the "connection to generator-specific shortcuts" are.
    • Line 163; it is not clear what low-dimensional structure is.
  • Because of the writing issues from the very beginning of the paper, the overall method section is very difficult to follow. As I understand, the main contribution of the authors is Eq. 4, but it is not clear exactly what this objective function is trying to do. For example, is this being used only for fake images or for real images too. Overall, the details being set aside, it should be somewhat easy for a reader to intuitively understand the main contribution of the work; something which is very much lacking right now.

  • The results are presented in a strange way. The authors are showing the results on multiple benchmarks (Table 1 - 6), but the baselines that are being compared to are changing in each table. Specifically, none of the baselines present in Table 1 which achieve competitive performance (sometimes even better) are present in Table 2. For example, PPL and HiDA-Net are not present in Table 2. If this is because the authors wished to show the performance of many baselines (and therefore splitting them into different tables), then that is not helpful. Because whether or not the competitive baselines from Table 1 remain competitive for other datasets should be made clear.

  • Following upon the previous point, the improvement in performance compared to the best baselines (PPL and HiDA-Net) is marginal in Table 1. Similar case is present in Table 4 as well. There is not much discussion about these marginal improvements; e.g., why the baselines perform so similarly, or sometimes even better. Furthermore, in Table 1, the performance of the proposed method differs a lot when using SigLIP2 vs CLIP. However, there is no discussion for why this happens.

  • Overall, there does not appear any meaningful take away from the results section because of very little analysis.

Questions for authors
  • Why is there a need of a RC-only phase in the joint training?

  • Why did you choose to use SigLIP2, in addition to CLIP? How/why should your method be sensitive to the choice of the encoder model?

  • Is Eq. 4 just cosine distance? If so, then the explanation can be made much more simpler (e.g., you can remove all occurrences of unit-normalized representations).

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

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