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Paper summary
This paper proposes PRISM, a unified post-hoc framework for attributing generated images to their source model. The attribution task is decomposed into two levels. Stage 1 identifies the model family using an autoencoder fingerprint built from the double reconstruction ratio ρRec, which the authors augment with the quantization error LQ and multiply into the family fingerprint for image autoregressive models (IARs). Stage 2 then localizes the specific version within the identified family using a latent generator fingerprint, namely an ELBO-based conditional log-likelihood for diffusion models (DMs) and token-level conditional log-probabilities for IARs. The authors evaluate 11 model families and 24 model versions, reporting 94.5% Macro-F1 for class-to-image attribution and 95.5% for text-to-image attribution, with family-level accuracies of 99.2% and 99.4%. The appendix adds experiments on robustness, open-world rejection, rejection of unseen versions, conditioning estimation, inference cost, and privacy-preserving collaborative auditing.
Critical strengths
The paper defines the task clearly, the two-level decomposition into family identification and version localization is reasonable, and the experimental coverage in the appendix goes beyond comparable post-hoc attribution work.
Critical weaknesses
- The binding between autoencoder type and generation paradigm is not verified, which undercuts the central claim of cross-paradigm unification. In Section 3.2 the paper states that the autoencoder is instantiated as a continuous VAE in diffusion models and as a VQVAE in IARs, and Section 3.3 uses this to determine the family fingerprint, so that DMs take LA = ρRec directly while IARs take LA = ρRec · LQ. However, the autoencoder type is not determined by the generation paradigm. Diffusion models with VQ or discrete latent autoencoders exist, and autoregressive models with continuous latent spaces also exist. More importantly, all 24 evaluated models in Table A1 fall inside this correspondence. The DM side consists entirely of continuous VAEs (SD1-VAE, SD2-VAE, SD3-VAE, SDXL-VAE, FLUX-VAE, VA-VAE, and SD-VAE), and the IAR side is built entirely on quantized or discrete tokenizers (MaskGIT-VQGAN, multi-scale VQVAE, and VQGAN-16384). The premise has therefore never been tested across the correspondence it assumes, even though applicability to both DMs and IARs is the headline claim of the paper. I also note that the paper hedges on the IAR side with "for most IARs" while making an unqualified assertion on the DM side. This asymmetry suggests that the premise has not been examined carefully.
- The evaluation set is constructed entirely by the authors and lacks a public benchmark, so the results cannot be compared with other work. Section 4.1 describes an evaluation set of 26,000 images generated by the authors, with 1,000 images per model across 24 models, and real images limited to 1,000 each from ImageNet and MS-COCO. No public benchmark for generated-image provenance is used anywhere in the paper, and no comparison is made against numbers reported in prior work. Because the authors re-implemented every baseline, gaps such as 94.5% versus 58.4% in Table 1 cannot be cross-checked against previously published values. In addition, the reference population for Grubbs' test, 250 images per class, and the evaluation images, the remaining 750 per class, are drawn from the same generation run and the same conditioning distribution. If the conditioning distribution shifts, for example toward prompt distributions found in the wild, the reported rejection rates are likely to be optimistic.
- The normality assumption behind Grubbs' test is verified only in a narrow setting. Appendix I.2 reports skewness for only nine autoencoder pairings, arranged as a 3 by 3 matrix, and all of them are measured on clean reconstruction distributions. One pairing, RAR-B against LlamaGen-L, has skewness 1.0132, which already exceeds the |skew| < 1 criterion that the authors adopt. Appendix E shows that strong augmentation substantially shifts the score distribution. At JPEG quality 60, for example, Macro-F1 drops to 81.9. Whether the Stage 1 rejection decision still holds under those conditions is not re-examined, even though the rejection mechanism depends directly on this normality assumption.
- Robustness and mechanism behavior are insufficiently validated in difficult settings. First, the robustness study in Appendix E covers only five conventional image transformations and is restricted to the RAR family with augmentation-finetuned encoders. It does not include compounding degradations such as repeated recompression, resizing, and screenshots applied in sequence, local edits such as cropping or inpainting, or adaptive adversarial perturbations designed by an attacker who knows the attribution method. The last of these is the most relevant threat model for a provenance method. Second, rejection of unseen versions is uneven within a family. LlamaGen-XL reaches only 71.1% at q = 1%, while FLUX derivatives sharing a single VAE are all above 99.9% under the same setting. The paper shows that the threshold is stable from q = 1% to q = 30% only for the FLUX case, offers no explanation for the degradation on the IAR side, and provides no operating-point trade-off curve. Third, Appendix D.2 shows that finetuning the encoder noticeably improves attribution, so the reported numbers depend on a one-time offline adaptation per family. The training-free claim in the main text should be scoped accordingly.
Questions for authors
- On the correspondence between autoencoder type and paradigm: how should LA be instantiated when a diffusion model uses a VQ or discrete autoencoder, for example a VQ-Diffusion or RQ-VAE style model, or when an autoregressive model uses a continuous latent space? Do the authors consider that this choice should be driven by the autoencoder type rather than by the generation paradigm? Could the authors add models that cross the current correspondence as a controlled comparison?
- On data and comparability: could the authors evaluate on a public benchmark for generated-image provenance, or at least provide a comparable comparison against numbers reported by prior work? In addition, could the Stage 1 rejection accuracy be re-verified using a reference population that is sampled independently of the query images and their conditioning distribution?
- On Grubbs' test: could the authors re-measure the skewness of the score distribution and the accuracy of the rejection decision under the augmentations used in Appendix E, for example JPEG quality 60 or a 0.5 times resize, and clarify whether the normality assumption still holds at those strengths? The specific effect of the RAR-B against LlamaGen-L pairing with skewness 1.0132 would also be helpful to understand.
- On robustness and version rejection: could the augmentation study be extended to all 24 model versions and supplemented with compounding degradations, local edits, and adaptive adversarial perturbations? For unseen-version rejection, could the authors provide a trade-off curve between the non-rejection rate and the false-rejection rate as the threshold q varies from 1% to 30%, and explain why LlamaGen-XL performs substantially worse?
- On privacy-preserving collaborative auditing: Appendix J specifies the full protocol and a conflict-resolution procedure, but only as a mechanism description. Could the authors provide a formal privacy guarantee or a measure of information leakage?
3 comments
Authors' Response (2/3)
Robustness (W4/Q4). In the following extensive table, we evaluate the robustness of our approach, across 21 settings spanning five perturbation types. With the augmentation-finetuned encoder, PRISM retains per-version F1 of 82.2–86.6 at JPEG quality 60 and 83.7–88.3 after 0.5× resizing. These results demonstrate that fine-grained attribution can remain effective after substantial post-processing without relying on a watermark.
We would like to further note that robustness against post-processing can be a very challenging aspect for provenance, which is hard even for methods that deliberately embed watermarks. Our approach faces the additional constraint of passive attribution: it must use existing model traces without modifying generation to protect them. The main focus of our paper is building a fine-grained, unified attribution method rather than making the method robust to all possible transformations. We will update more results for robustness evaluation in the camera-ready version.
Table R2. Robustness to post-processing, by augmentation type and strength. We report F1 per model version with the augmentation-finetuned encoder.
| Augmentation | Strength | RAR-B | RAR-L | RAR-XL | RAR-XXL | Macro-F1 |
|---|---|---|---|---|---|---|
| None | — | 94.5 | 95.0 | 95.5 | 94.7 | 96.2 |
| JPEG | q=90 | 93.5 | 92.1 | 94.3 | 92.6 | 93.4 |
| JPEG | q=80 | 91.6 | 90.9 | 92.7 | 90.2 | 90.4 |
| JPEG | q=70 | 89.0 | 85.2 | 90.3 | 88.1 | 86.8 |
| JPEG | q=60 | 86.5 | 82.2 | 86.6 | 82.7 | 81.9 |
| Resize | ×0.9 | 94.5 | 94.7 | 96.4 | 94.6 | 96.2 |
| Resize | ×0.8 | 93.5 | 93.2 | 95.2 | 93.3 | 95.2 |
| Resize | ×0.7 | 93.6 | 94.0 | 95.6 | 92.9 | 94.9 |
| Resize | ×0.6 | 91.9 | 91.0 | 94.5 | 90.5 | 92.7 |
| Resize | ×0.5 | 86.5 | 83.7 | 88.3 | 84.6 | 84.4 |
| Gaussian blur | r=0.5 | 94.8 | 94.9 | 96.0 | 94.7 | 96.4 |
| Gaussian blur | r=1.0 | 91.6 | 92.2 | 95.1 | 91.8 | 93.0 |
| Gaussian noise | std=1 | 94.1 | 93.9 | 95.3 | 93.6 | 95.3 |
| Gaussian noise | std=2 | 93.9 | 93.1 | 94.6 | 92.9 | 94.2 |
| Gaussian noise | std=3 | 92.0 | 92.0 | 93.3 | 91.1 | 92.2 |
| Gaussian noise | std=4 | 92.0 | 90.7 | 92.8 | 89.7 | 90.5 |
| Gaussian noise | std=5 | 90.1 | 87.9 | 90.1 | 88.4 | 87.4 |
| Saturation | ×1.1 | 94.5 | 94.1 | 95.3 | 94.4 | 95.5 |
| Saturation | ×1.2 | 93.1 | 93.7 | 94.4 | 93.4 | 93.6 |
| Saturation | ×1.3 | 91.5 | 91.2 | 93.1 | 92.2 | 91.1 |
| Saturation | ×1.4 | 89.2 | 88.4 | 90.5 | 89.5 | 87.3 |
| Saturation | ×1.5 | 85.7 | 85.1 | 87.0 | 86.0 | 82.9 |
Unseen versions (W4/Q4). PRISM checks how decisively the top-scoring version beats the runner-up. It returns “family known, version unknown” when this margin falls below the q-quantile of margins on the winner’s own calibration images. Increasing q raises the threshold, rejecting more unknown images at the cost of more false rejection.
The LlamaGen-XL result reflects the remaining candidates. With XL held out, every XL image scores higher under L than B, and 28.9% retain a margin above the q = 1% threshold. FLUX leaves six siblings, whose top two scores are typically nearly tied, making rejection easier.
Table R3 shows the trade-off. At q = 5%, XL rejection rises from 71.1% to 89.3%. Across LlamaGen leave-one-out settings, average rejection rises from 89.6% to 96.4%, while false rejection increases from 1.9% to 6.7%.
Table R3. Unknown-version rejection and false rejection as q varies. Each version is held out in turn and tested on its 750 query images. All rates are percentages, rounded to one decimal place.
| Metric (%) | q=1% | q=2% | q=5% | q=10% | q=20% | q=30% |
|---|---|---|---|---|---|---|
| FLUX: unknown-version rejection | 100.0 | 100.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| FLUX: false rejection | 1.3 | 2.8 | 6.8 | 12.7 | 24.4 | 34.8 |
| LlamaGen: unknown-version rejection | 89.6 | 91.1 | 96.4 | 97.9 | 99.3 | 99.6 |
| LlamaGen: false rejection | 1.9 | 3.2 | 6.7 | 11.8 | 21.5 | 31.2 |
| LlamaGen-XL held out: rejection | 71.1 | 74.1 | 89.3 | 93.7 | 98.0 | 98.8 |
| Family rows are averages over leave-one-version-out settings. False rejection is measured among correctly attributed enrolled images within those settings. |
If our response addresses your concerns, we would greatly appreciate it if you could consider raising the score. Thank you!
Authors' Response (3/3)
Privacy guarantee (Q5). We formalize the information disclosed by the collaborative protocol in Appendix J.
Guarantee. Let P denote public protocol parameters and θ the owners’ private model weights, reference data, and calibration statistics. For a query x, define the disclosed output L=(r_1,...,r_m,b_1,...,b_t), where each r_i is an owner’s categorical response and each b_j is a disclosed conflict-comparison outcome. Assume an honest-but-curious coordinator that does not collude with owners, sequentially executed comparisons with simulation security for the coordinator’s visible messages, and communication schedules and message lengths determined by P, x, and L.
Let View_C(P,x,θ) denote the coordinator’s view in a real execution, including its inputs, random coins, and received protocol messages. There exists a probabilistic polynomial-time algorithm Sim that takes only P, x, and L, has no access to θ, and outputs a simulated coordinator view such that
View_C(P,x,θ) ≈c Sim(P,x,L).
Here, ≈c denotes computational indistinguishability. Thus, the coordinator learns no additional computationally accessible information about the private state beyond the disclosed outputs.
Proof. We construct Sim(P,x,L) as follows. The simulator samples the coordinator’s random coins according to the protocol and reproduces the query-distribution messages. It then inserts the categorical replies r_1,...,r_m supplied in L. These messages are reproduced exactly. Autoencoder evaluation, generator scoring, and calibration are local computations and contribute no further messages.
For each conflict comparison, the simulator uses the comparison protocol’s simulator with its public parameters and disclosed outcome b_j. The communication schedule and message lengths are reproducible from the stated inputs. Consider hybrid transcripts that replace real comparison executions with these simulated executions one at a time. Any efficient distinguisher between two adjacent hybrids would distinguish a real comparison execution from its simulation, contradicting the assumed comparison security. Since the protocol uses polynomially many sequential comparisons, the sum of these distinguishing advantages is negligible. The simulator outputs the assembled coordinator view. The first hybrid is the real coordinator view and the last is the distribution of Sim(P,x,L). This proves the claimed computational indistinguishability.
Authors' Response (1/3)
Thank you for your constructive feedback! We address your main concerns as follows.
Architecture and training (W1/Q1). The quantizer determines whether a quantization error is available. For example, a VQ diffusion model could use the quantized Stage 1 fingerprint, and a continuous-latent AR model could use the reconstruction ratio with a continuous generator score in Stage 2. Table A1 covers continuous-autoencoder DMs and discrete-tokenizer IARs. The source generator stays fixed, and the scoring encoder can be adapted offline.
Benchmark and calibration (W2/Q2). As far as we understand, there are no comprehensive benchmarks that cover all the models we evaluate. Therefore, we construct this benchmark for the provenance task, which is also one of our contributions to the community. Every method faces the same checkpoints and held-out images, making Table 1 a controlled version-attribution comparison.
Gaussian assumption (W3/Q3). PRISM’s central contribution is the selection and combination of complementary autoencoder and generator signals for fine-grained attribution. We chose Grubbs test as an instantiation of the statistical test, but the specific test is replaceable. In particular, a KDE-based autoencoder compatibility test estimates the reference-score distribution without requiring Gaussianity. We evaluated a KDE-based variant of PRISM. As shown below, it yields attribution recall close to the original Grubbs-based implementation across the 13 evaluated generators, while maintaining real-image rejection rates of 97.6% on ImageNet and 98.9% on MSCOCO. This supports the use of PRISM’s attribution signals with an alternative autoencoder compatibility test that does not require Gaussian reference distributions.
Table R1. Grubbs versus KDE on the class-to-image pool. The results for Grubbs test correspond to Figure 3a in the paper.