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- Confidence
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- Informativeness
- 2
- Presentation
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- Soundness
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Paper summary
The paper asks whether the fine-tuning recipe of a text-to-image diffusion model can be recovered from its generated images alone, under black-box query access. The attack builds shadow models with known recipes, summarises each model's generations into a behavioural fingerprint, trains supervised predictors on fingerprint-recipe pairs, and applies them to unseen victims.
The fingerprint is a 78-dimensional vector over seven blocks: base-model drift, output diversity, prompt-perturbation sensitivity, texture, text-image alignment, cross-prompt consistency and colour, instantiated separately with frozen DINOv2, CLIP and DeiT. The primary bank is 297 SD v1.5 LoRA models fine-tuned on an 833-image Pokemon corpus over a six-hyperparameter grid -- rank {4,16,64}, alpha {8,16,32}, learning rate, batch size, steps, dropout -- probed with 96 prompts and eight seeds. Predictors are RF, XGBoost, logistic regression and two MLPs, evaluated under three-fold, ten-repeat model-level cross-validation stratified by rank, with a fixed 300-tree RF as a selection-independent reference, three baselines, and 1,000-permutation tests with Benjamini-Hochberg correction.
Rank is recovered at 85.4% against a 34.4% stratified baseline, scaling at 72.8%, and learning rate, steps and batch at 49-56%; dropout is weak and predictor-dependent. Exact six-component joint recovery is 9.6-10.2% against a 0.21% uniform-chance baseline. Rank generalises off-grid (100% bracketing of six unseen ranks, Spearman rho about 0.81) and transfers across SD 2.1, changed base weights, a different domain and a disjoint same-domain corpus. Eight prompts yield 82.9% rank accuracy under pooled cross-validation with predictor selection. Nineteen non-adaptive output-perturbation settings only partially reduce rank recovery, and the adaptive setting is explicitly left unevaluated. Adapter-drift controls show norms alone predict rank at 99.9%, while drift-stratified and residualised behavioural features retain most of the signal.
Critical strengths
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The evaluation includes several statistical controls that make the claims assessable. Model-level rather than image-level cross-validation, stratified by rank, with preprocessing fit only on training folds; three distinct baselines; a fixed 300-tree RF reported alongside the best predictor so the headline does not silently depend on model selection; 1,000-permutation tests with Benjamini-Hochberg correction; and an explicit statement that the procedure does not correct for selection among five predictors, so best-of-five results are exploratory. Per-predictor q-values are given for the borderline dropout result instead of a single convenient number. The checked recovery-rate and grid calculations reconcile; the permutation p-value in Table 8 requires clarification.
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The characterisation of what leaks is fine-grained and honest, and the empirical investment is substantial. Leakage is reported as heterogeneous: rank strong and transferring across architecture, base weights, domain and a disjoint corpus; scaling partial; learning rate, steps and batch clearly above chance but much weaker; dropout correctly de-emphasised. Off-grid behaviour is framed as bracketing and ordering rather than exact recovery. The guidance-5.0 degradation, the non-monotonic transition between ranks 24 and 32, and the systematic confusion structure are all reported, and the discussion states plainly that the findings "establish predictive associations rather than a causal mechanism". Roughly 627 fine-tuned models is a serious amount of controlled compute.
Critical weaknesses
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The predictive association is supported, but the mechanism underlying rank recovery remains unresolved, limiting our understanding of generalization beyond the evaluated settings. Adapter norms alone identify rank at 99.9% -- higher than the behavioural fingerprint's 85.4% -- while the residualisation control removes only the linear association with a single scalar (85.4% to 82.7%); the paper concedes that "other relationships with adapter-update magnitude may remain". ||B|| is also not the right quantity to control for: B -> cB, A -> A/c leaves BA unchanged while changing ||B||, and the deployed update is (alpha/r)BA. The paper does define and use base-model drift features, so drift is not unmeasured; what is absent is a control that MATCHES effective-update norm or measured drift across ranks and then re-tests recovery. The feature ablation points the same way: all seven blocks independently reach 78.9-86.2%, leave-one-out never falls below 84.0%, and the 12-dimensional colour block (86.2%) edges out the full fingerprint (85.4%) with no significance test on the gap. That redundancy is at least consistent with one dominant latent factor measured seven ways. This does not make the rank signal spurious and does not undercut a predictive association on held-out models within a stated distribution; it limits the rank-specific mechanistic reading the title invites.
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The demonstrated claim is narrower than the framing, and the defence study is non-adaptive. Recovery is strongly heterogeneous: rank 85.4% and scaling 72.8% against 33.3% chance; learning rate 54.4%, steps 55.9% and batch 49.4% well above chance but much weaker; dropout 55.0% against a 53.8% majority baseline. Joint six-component recovery is 9.8%, so the defensible summary is around 10% exact full-recipe recovery with markedly uneven per-component performance. What is most solidly established is rank, a three-way choice on a log-spaced grid where adjacent classes differ by 4x and the endpoints by 16x, in the primary controlled protocol, with additional transfer experiments extending beyond its training domain and base model. Off-grid, the log2-rank MAEs of 0.682/0.691/0.708 give a geometric-mean multiplicative error around 1.60-1.63x -- a useful average error scale, not a prediction interval with stated coverage. Most consequentially, the perturbation defences are applied only to victim outputs while the attacker's predictors are never retrained, and Appendix E.1 says so: the reported figures are rank-recovery accuracies under a fixed attacker, not suppression rates (46.2% under x0.125 downscaling, 51.6% under strong quantisation, 54.8% under JPEG q10), and effectiveness against an adapted attacker remains untested. This limits the deployment-facing conclusions; it does not undercut the black-box leakage evidence itself.
Questions for authors
Items 1-3 would move my score; the rest are secondary.
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(Experiment request) Can you separate rank from update magnitude? Compensate alpha or the training budget so that rank-4, rank-16 and rank-64 adapters reach a matched effective-update norm ||(alpha/r) B A|| or matched measured base drift, then re-run behavioural rank recovery on that bank. Residualising log||B|| does not remove the confound, since B -> cB, A -> A/c leaves BA unchanged. This would test whether rank recovery persists after controlling these quantities, although it would not by itself establish a causal mechanism; I consider it the most valuable addition.
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(Experiment request) Please evaluate the adaptive defence setting: train shadow predictors on perturbed shadow generations matched to the victim's perturbation, then attack perturbed victims. No new diffusion models are needed. Measuring the adaptation cost would also tell deployers how much protection they actually have.
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(Clarification) Please discuss Asnani et al., "Reverse Engineering of Generative Models: Inferring Model Hyperparameters from Generated Images" (arXiv:2106.07873; IEEE TPAMI 2023), which shares the paradigm -- a fingerprint from generated images, fed to a trained predictor, used to infer generative-model hyperparameters across a bank of models -- and is not cited. It targets GAN architecture and loss choices rather than diffusion fine-tuning recipes, and your claim is already scoped to text-to-image diffusion, so I am not asking you to retract it; I am asking for explicit positioning so readers can see which part of the paradigm is inherited and which is new.
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(Clarification) Appendix C.4 describes 1,000 permutations with an add-one correction, whose smallest attainable p-value is 1/1001 = 0.000999, yet Table 8 reports p = 0.0007. Did that table use a different test, more permutations, or an exact procedure? Raised only to get the procedure on record.
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(Clarification) How do results change on a finer grid -- ranks {4,8,16,32,64}, alpha over a narrower range, adjacent learning rates within 2x? Adjacent rank classes currently differ by 4x and the endpoints by 16x. Would within-grid log-space regression be a more representative headline than three-way classification? Could you also report the per-rank error distribution and error quantiles for the off-grid result, since a mean multiplicative error does not tell a reader how tight any individual prediction is?
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(Clarification) Section 5.9 already notes that the 8-prompt figure uses the best-performing predictor under pooled cross-validation and is not validated on independently held-out victims, which I appreciate. Could you add the matched comparison under the fixed 300-tree RF and the main protocol?
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(Clarification) Which fingerprint components carry the cross-setting transfer -- the encoder-agnostic pixel blocks or the base-drift features, which need the correct base checkpoint? The architecture-blind result, where DINOv2 drops from 78.3% to 60.1% while CLIP and DeiT hold at 74.6% and 71.6%, suggests the blocks behave differently. Relatedly, at guidance 5.0 the selected random forest never predicts rank 4 at all (Table 16: the rank-4 column is 0/0/0 across 675 predictions). Which feature block drives that one-directional shift?
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(Suggestion, optional) Releasing the fingerprint extractor and the fingerprint-label bank, plus per-model recipe and split manifests, the 96 prompts, and per-model out-of-fold predictions, would let readers check the predictors without needing model weights.
2 comments
Response to Reviewer aXP1 (Part 2)
Q4. Permutation p-value in Table 13.
We thank the reviewer for identifying this discrepancy. Table 13 uses a different permutation procedure from the cross-validation test: we permute the nine victims' labels against fixed predictions from the first seeded classifier fit, without retraining, using 10,000 permutations and an add-one correction. The minimum attainable Monte Carlo p-value is therefore , rather than .
The nine victims comprise three models per rank. Under permutations preserving these class counts, perfect rank recovery has an exact null probability of , consistent with the reported Monte Carlo estimate ().
We have clarified the permutation procedure and evaluation protocol in Appendix C.5 and the caption of Table 13.
Q5. Off-grid rank error distribution.
We thank the reviewer for requesting a more detailed characterization of off-grid rank errors. We analyzed predictions for 48 victims at six unseen ranks (6, 8, 12, 24, 32, 48) under the original evaluation protocol.
For DINOv2, the median absolute error is 0.60 log₂-rank units (approximately 1.5× multiplicative error). 77% of predictions fall within a factor of two, with a 90th-percentile error of approximately 2.5× and a maximum observed error of 2.6×. CLIP and DeiT show similar distributions, with maximum errors below 2.8×.
The overall signed bias is small (+0.04 log₂ for DINOv2), although rank 24 tends to be overestimated and rank 32 underestimated, consistent with the non-monotonicity in Fig. 2. Since the regressor is trained on only three rank values, these results support approximate rank estimation rather than calibrated continuous prediction.
We have added the per-rank error distribution and scaling analysis to Section 5.4 and Appendix C (Table 8).
Q6. Fixed-predictor and held-out evaluation of the 8-prompt result.
We repeated the 8-prompt evaluation using a fixed 300-tree random forest, without predictor selection, under pooled model-level cross-validation (297 models) and independent held-out evaluation (162 shadows, 135 victims). Results are averaged over 20 random prompt subsets.
| Hyperparameter | Pooled CV (8 prompts) | Held-out (8 prompts) | Held-out (96 prompts) |
|---|---|---|---|
| LoRA rank | 82.6 ± 1.1% | 78.0 ± 2.7% | 77.9% |
| LoRA scaling | 65.6 ± 3.2% | 59.6 ± 4.5% | 67.9% |
For comparison, the original best-of-five pooled-CV rank result was 82.9 ± 1.1%. All 20 eight-prompt subsets achieve significant held-out rank recovery (permutation ).
Thus, low-budget rank recovery persists without predictor selection and on independently held-out victims. Scaling is more sensitive to prompt reduction, so we restrict the strongest 8-prompt claim to rank.
We have added these results to Section 5.9 and Appendix D.3.
Q7. Feature-block transfer and rank-4 collapse under CFG 5.0.
We conducted additional feature-block ablations using a fixed 300-tree random forest to examine transfer robustness and guidance-dependent rank recovery.
Feature-block transfer. Under SD v2.1 architecture transfer, removing the base-drift block improves architecture-blind rank recovery:
| Encoder | Full fingerprint | Without base drift |
|---|---|---|
| DINOv2 | 55.7% | 72.5% |
| CLIP | 62.0% | 75.9% |
| DeiT | 71.6% | 77.8% |
Pixel-only features achieve 69.0% across all three encoders. Under data shifts, block contributions vary, with base-drift features helping in some settings but degrading recovery in others. These results indicate that transferable rank information is not confined to a single fingerprint block (see Appendix C, Table 15).
Rank-4 collapse at CFG 5.0. We compare rank-4 recall from individual fingerprint blocks:
| Fingerprint block | CFG 7.5 | CFG 5.0 |
|---|---|---|
| Base drift | 82% | 17% |
| Diversity | 12% | 0% |
| Cross-prompt consistency | 98% | 97% |
| Colour | 100% | 93% |
Reduced guidance substantially weakens rank-4 recovery from some blocks, while cross-prompt consistency and color remain informative. Thus, the effect is feature-dependent rather than a uniform loss of rank information. These single-block ablations do not establish which features cause the full classifier's rank-4 collapse (see Appendix D.6, Table 26).
Q8. Release of the fingerprint extractor and evaluation artifacts.
We have prepared an anonymized reproducibility package containing the fingerprint extractor, fingerprint–label banks, recipe and split manifests, 96 probe prompts, and per-model out-of-fold predictions. The package includes scripts to reproduce the primary results without model weights or generated images. An anonymized repository link is provided in the revised manuscript's Reproducibility Statement.
Response to Reviewer aXP1 (Part 1)
We thank the reviewer for their constructive feedback. We have addressed the concerns through additional experiments and manuscript revisions, with all changes highlighted in blue. Our point-by-point responses follow.
Q1. Separating rank from effective-update magnitude.
We thank the reviewer for highlighting this confound. We agree that the norm of the LoRA B matrix is insufficient, as reciprocal rescaling of the LoRA factors leaves the effective update unchanged. We therefore measure the aggregate Frobenius norm of the effective update: ΔWℓ=rαBℓAℓ
\sqrt{\sum_{\ell} \lVert \Delta W_{\ell} \rVert_F^2}$$ We match rank-4/16/64 adapters from our 297-model collection within 0.15 decades of log effective-update norm, without using behavioral features or prediction outcomes. This yields **64 matched triplets (192 models)** and reduces the maximum cross-rank standardized mean difference in log norm from **0.97 to 0.11**. Using DINOv2 fingerprints, a fixed 300-tree random forest, and 3-fold × 10-repeat model-level cross-validation, rank recovery remains **85.2% (permutation p = 0.001)**, compared with 85.4% on the original collection. On the same matched cohort, update norm alone achieves **44.4%**, while update norm combined with the remaining recipe components achieves **52.9%**. Behavioral fingerprints outperform the combined control by **32.3 percentage points (95% paired bootstrap CI: 25.4–39.3)**. These findings demonstrate that measured effective-update magnitude and the remaining recipe components do not fully explain behavioral rank recovery. While matching does not establish a causal mechanism or eliminate all update-related confounds, the rank signal persists after substantially reducing the proposed confound. We have added the matching protocol, controls, and statistical results to **Section 5.8 and Appendix C.14**. **Q2. Adaptive attacker against output-perturbation defenses.** We thank the reviewer for this suggestion. We evaluate a defense-aware attacker that applies the same perturbations to its 162 shadow-model outputs, re-extracts DINOv2 fingerprints, and retrains the fixed 300-tree random forest. Evaluation uses the same 135 independently held-out victims as the non-adaptive setting. At the strongest tested setting of each defense, we obtain: | Perturbation | Non-adaptive | Adaptive | |:-------------|-------------:|---------:| | Downscaling (0.125×) | 46.2% | **79.6%** | | Quantization (6 bits removed/channel) | 51.6% | **79.6%** | | JPEG (quality 10) | 48.9% | **79.4%** | | Gaussian noise (32/255) | 75.1% | **80.7%** | The undefended baseline is **77.9%**. Across all four perturbations, adaptive recovery reaches **79.4–80.7%**, indicating that the non-adaptive reductions largely reflect train–test distribution mismatch rather than elimination of recoverable rank information. Adaptation requires no additional diffusion-model training, only reprocessing existing shadow outputs and retraining the predictor. We have added the adaptive evaluation to **Section 5.10 and Appendix E**. The tested perturbations do not reduce rank recovery below the undefended baseline against a defense-aware attacker. **Q3. Positioning relative to Asnani et al.** We thank the reviewer for highlighting this relevant work. We agree that Asnani et al. (TPAMI 2023) established the broader model-parsing paradigm, including diffusion-model experiments. We have added the citation and clarified our positioning in Related Work. Our work differs in its target and experimental setting: rather than inferring generator architecture or training loss, we investigate **fine-tuning-recipe leakage** in text-to-image diffusion models. We hold the base checkpoint, architecture, and training corpus fixed while varying six LoRA hyperparameters, and recover these properties using model-level behavioral fingerprints aggregated across controlled prompts and seeds. We additionally adapted the authors' official FEN+PN implementation to predict our six recipe components, using the same 297 models, query budget, and 3-fold × 10-repeat model-level cross-validation splits: | Hyperparameter | Ours | FEN+PN | |:---------------|-----:|-------:| | LoRA rank | **85.4%** | 79.2% | | LoRA scaling | **72.8%** | 64.2% | | Batch size | **49.4%** | 40.0% | | Training steps | **55.9%** | 51.8% | All four improvements are significant after Benjamini–Hochberg correction. Learning rate and dropout show no significant differences. This comparison evaluates complete inference pipelines rather than fingerprint representations in isolation. Our contribution is therefore not the general paradigm of model parsing, but the **systematic characterization of fine-tuning-recipe leakage in text-to-image diffusion models**, supported by a direct comparison with prior work. We have incorporated the comparison into the **Section 5.2 and Appendix C.3**.