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Under review as a conference paper at ICLR 2027

Radioactive Watermarking of Graph Node Classification Datasets for Scalable Owner Attribution

Abstract

Graph datasets used in industrial graph neural network (GNN) applications are valuable proprietary assets, often licensed to multiple buyers under restricted-use agreements. When a suspect GNN trained on a buyer's leaked dataset copy appears, the owner must identify the responsible buyer, since only buyer-level attribution allows terminating the license and pursuing legal remedies. However, this task is unsupported by existing dataset watermarks which provide only binary ownership verification and fail under multi-buyer owner tracing. In this paper, we introduce the first radioactive watermarking method for graph node classification datasets that supports scalable owner attribution. Radioactive means that the watermark signal persists through training and is recoverable from model outputs, without access to the released data, the buyer's training procedure, or the GNN architecture. Detection is therefore architecture-agnostic and black-box, meaning it can be applied to suspect models with different architectures, and the underlying test is a closed-form statistic with a provably bounded false-positive rate, jointly protecting dataset and model intellectual property. We attribute a leaked suspect to its true buyer at marketplace scale via a per-buyer watermarking test, with a closed-form attribution rate that saturates with the number of buyers. Across five benchmarks and eight GNN architectures, our method achieves a stealthy yet highly detectable watermark signal that remains robust under cross-architecture detection and four removal attacks, while incurring negligible degradation in task accuracy, and provides reliable owner traceability at the scale of multi-buyer data marketplaces.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Graph watermark, owner attribution, graph neural networks

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

The paper considers a data owner who licenses a graph node classification dataset to many buyers under terms that forbid redistribution. If a model trained on a leaked copy appears, the owner only has access to that model, and wants to determine both whether it was trained on their data and which buyer's copy was used.

Each buyer receives a personalised copy, and the owner has a secret key consisting of one random unit vector per class for each copy of the data that the owner sent out. The owner perturbs the features of a small set of nodes so that their representations in a frozen one-layer linear GCN surrogate (trained on the clean data) shift towards the key vector for their class; edges and labels are left unchanged.

To detect the watermark, the owner fits a least-squares map from the surrogate's representations to the suspect's on clean nodes, keeps and whitens the shared directions of this map, and compares each class's classifier weight with the translated key. Each class gives a p-value under the null that the key is a random direction, and these are combined using Fisher's method. For attribution, the test is run with every buyer's key and the buyer with the smallest p-value below a Bonferroni-corrected threshold is blamed. In the black-box setting, the owner first selects the most likely buyer copy with a loss-gap test, distills a student model from the suspect's outputs, and runs the same test on the student.

The claimed contributions are:

  • the first radioactive watermark for graph node classification datasets that supports attribution across many buyers,
  • a design-time condition for detection success (Corollary 1), and
  • an approximate closed-form attribution success rate (Corollary 2).

The method is evaluated on five datasets (three homophilic, two heterophilic) with 1,000 buyers, 50 watermarked and 50 clean suspects per setting, and a 1% accuracy budget, using 2-layer GCN suspects in the main results and eight suspect architectures on ogbn-arxiv and Roman-Empire. The white-box variant achieves 100% detection and attribution accuracy on four datasets and the black-box variant 92-98% detection accuracy, with Amazon-Ratings (5 classes) as the exception. The method outperforms the baselines, the strongest being Data Taggants, and the appendix reports robustness to random noise, pruning, fine-tuning, and distillation.

Critical strengths
  1. The paper addresses a relevant gap. Existing dataset watermarks that can be verified from a trained model only answer whether the owner's data was used, and cannot attribute a leak to a specific buyer, even though buyer-level attribution is what makes a restricted-use license enforceable. The threat model, where the owner only has access to the trained model and not the data used, is realistic. This is consequential because it moves dataset watermarking from yes/no ownership checks to a setting that matches how datasets are actually licensed.

  2. There are strong empirical results. With 1,000 buyers, the white-box variant achieves 100% detection and attribution accuracy on four of the five datasets, and clearly outperforms Data Taggants, the strongest baseline and the only external one built on per-buyer private keys, on ogbn-products (100/100 vs 64/20 WDA/OAA) and Reddit (100/100 vs 51/2). This is consequential because it shows that key-based attribution works at marketplace scale where the closest alternative breaks down.

Critical weaknesses
  1. Collusion between buyers seems like a natural attack in this marketplace setting: two or more buyers could compare copies to locate the perturbed nodes, or average them to weaken each watermark. It would be useful to evaluate how detection and attribution hold up under such attacks.

  2. The paper claims a provably bounded false-positive rate: a model never trained on a watermarked copy should be flagged with probability at most τ = 0.05 across all B keys (Eq. 13, Appendix C.3), and Appendix F states that this also holds for the black-box variant. False-positive rates are not reported alongside Tables 1, 22, and 23 (the only figure at the B = 1000 threshold is a pooled 0/250 check in Appendix D.5), but they can be inferred: OAA counts a watermarked suspect only if it is flagged (Eq. 5), so when OAA is 100%, every WDA error must be a clean suspect that was wrongly flagged. By this reasoning, Table 22 (black-box, GIN-2L on ogbn-arxiv: 86% WDA, 100% OAA) implies that 14 of 50 clean suspects were flagged (28%), ResGCN-8L implies 11 of 50, and Table 1 (black-box, ogbn-arxiv) implies 6 of 50, all above the 5% bound. Could you report false-positive and true-positive rates separately for every B = 1000 setting, with confidence intervals, and explain these cases? From this, the guarantee does not appear to hold.

  3. In the black-box setting, Stage 1 selects a buyer's copy with the loss-gap test before the watermark test is run, and the student is distilled on that copy. How often does the final attribution differ from Stage 1's choice, and what is the attribution accuracy of Stage 1 alone at B = 1000?

Questions for authors
  1. The paper claims a provably bounded false-positive rate: a model never trained on a watermarked copy should be flagged with probability at most τ = 0.05 across all B keys (Eq. 13, Appendix C.3), and Appendix F states that this also holds for the black-box variant. False-positive rates are not reported alongside Tables 1, 22, and 23 (the only figure at the B = 1000 threshold is a pooled 0/250 check in Appendix D.5), but they can be inferred: OAA counts a watermarked suspect only if it is flagged (Eq. 5), so when OAA is 100%, every WDA error must be a clean suspect that was wrongly flagged. By this reasoning, Table 22 (black-box, GIN-2L on ogbn-arxiv: 86% WDA, 100% OAA) implies that 14 of 50 clean suspects were flagged (28%), ResGCN-8L implies 11 of 50, and Table 1 (black-box, ogbn-arxiv) implies 6 of 50, all above the 5% bound. Could you report false-positive and true-positive rates separately for every B = 1000 setting, with confidence intervals, and explain these cases? From this, the guarantee does not appear to hold.

  2. In the black-box setting, Stage 1 selects a buyer's copy with the loss-gap test before the watermark test is run, and the student is distilled on that copy. How often does the final attribution differ from Stage 1's choice, and what is the attribution accuracy of Stage 1 alone at B = 1000?

Reviewer_9J4sOpenReview ↗
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Paper summary

The paper studies buyer attribution when a dataset owner distributes differently watermarked copies of a graph dataset. It perturbs selected node features so that their embedding shifts align with private class-specific directions. A suspect model is tested by transporting those directions into its representation space, comparing them with classifier weights, and combining the evidence across classes. The paper also proposes black-box verification through student distillation and evaluates attribution among 1000 buyer keys. I appreciate the distinction between detecting unauthorized dataset use and identifying the buyer whose copy was used. The experiments are extensive, and several reported results are strong. However, the statistical guarantees are central to the contribution, and I found problems in the detection derivation and the calibration of the black-box procedure. The attribution approximation and baseline comparison also need clarification.

Critical strengths

The attribution problem is meaningful. Identifying one buyer among many is a useful extension beyond binary dataset ownership verification. The setup clearly explains why detection alone does not answer the intended question.

The geometric design is reasonable. Class-specific feature perturbations leave the graph topology unchanged. Aligning the surrogate and suspect representation spaces before comparing carrier directions and classifier weights addresses a real obstacle to transfer across architectures. The whitening step also accounts for unequal scaling in the fitted alignment map.

The empirical work is extensive. The paper includes five datasets, eight architectures, four removal attacks, buyer-count sweeps, several component studies, and runtime measurements. Under the stated utility budget, Table 1 reports perfect white-box detection and attribution on four datasets. The authors also report weaker results on Amazon-Ratings and the utility cost of increasing its watermark strength. These results provide useful evidence about both the method's performance and its limits.

Critical weaknesses

1. The detection certificate relies on an incorrect Fisher-combination identity and an unsupported concentration bound.

Appendix D.5 correctly defines Fisher's statistic in Eq. (25): for CC classes with per-class p-values pcp_c, the statistic is T=−2∑c=1Cln⁡pcT=-2\sum_{c=1}^{C}\ln p_c, and the combined p-value is pFisher=Pr⁡(χ2C2≥T)p_{\mathrm{Fisher}}=\Pr(\chi^2_{2C}\ge T). However, Eq. (31) then identifies −ln⁡pFisher-\ln p_{\mathrm{Fisher}} with ∑c(−ln⁡pc)\sum_c(-\ln p_c). These quantities are not equal: the latter is the negative log of the product of the class p-values, whereas the former requires evaluating the chi-square survival function.

For example, with three classes and pc=e−1p_c=e^{-1} for each class, Fisher's statistic is T=6T=6 and the combined p-value is 8.5 e−3≈0.42328.5\,e^{-3}\approx0.4232. Thus, the combined negative log p-value is −ln⁡pFisher=3−ln⁡(8.5)≈0.860-\ln p_{\mathrm{Fisher}}=3-\ln(8.5)\approx0.860, whereas the sum of the class negative log p-values is ∑c(−ln⁡pc)=3\sum_c(-\ln p_c)=3.

The residual in Eq. (32) contains corrections to the individual class log p-values but does not include the missing Fisher survival-function correction. Although the text before Eq. (33) invokes a −C/2-C/2 "Fisher Stirling" correction, it does not derive that expectation or reconcile it with the residual explicitly defined in Eq. (32). Consequently, the expectation formula in Eq. (33) and the detection-success condition in Corollary 1 are not established by the derivation as written.

There is a separate issue with the concentration argument. Let δB\delta_B denote the claimed failure probability. Equation (36) uses a sample standard deviation multiplied by 2ln⁡(1/δB)\sqrt{2\ln(1/\delta_B)} as an empirical Bernstein margin for a future suspect's detection statistic. The proof does not establish assumptions sufficient for this tail bound or account for uncertainty in estimating the variance from a finite number of calibration suspects. A valid concentration statement needs to specify its distributional assumptions and finite-sample correction.

These issues affect the claimed design-time guarantee of detection success on future suspects. They do not necessarily invalidate the implemented white-box hypothesis test if its p-values are correctly computed and the required null assumptions hold. The paper should distinguish false-positive control under the null from guaranteed detection power under the alternative.

2. False-positive control is not established for the complete black-box procedure.

Appendix F selects a buyer-specific watermarked dataset only when the largest loss gap exceeds 0.5; otherwise it selects the benign dataset. A student trained entirely through a key-independent benign-data procedure could retain the white-box null. However, the paper does not establish false-positive control for the complete pipeline, including incorrect selection of a watermarked dataset for a benign suspect. The inputs and loss terms used after the benign fallback also need to be specified. The claim that subtracting original-input logits removes carrier dependence does not by itself establish the required null distribution.

The reported metrics raise a related concern. Table 22 gives 86% WDA and 100% OAA for black-box GIN-2L on ogbn-arxiv, using 50 watermarked and 50 benign suspects. Under Eq. (5), attribution success requires both detection and correct buyer identification. Therefore, if the reported metrics follow Eq. (5) and use the stated common evaluation pool, 100% OAA means that all 50 watermarked suspects were correctly detected. The 14 detection errors implied by 86% WDA must then occur among the 50 benign suspects, giving an empirical false-positive rate of 14/50=28%14/50=28\%. The calculation does not identify the cause, but the reported rate needs to be reconciled with the claimed 5% familywise level.

Appendix C.3 states that the experiments use the Bonferroni-corrected threshold, consistent with Eq. (13). However, Algorithm 3 does not specify whether its input threshold has already been corrected. Please make the pseudocode consistent with the experimental description and confirm that the reported black-box results use the corrected threshold.

The authors should establish or empirically calibrate false-positive control after the complete selection-and-distillation procedure, and report confusion counts and end-to-end false-positive rates separately for white-box and black-box verification.

3. The attribution formula depends on modeling assumptions whose range of validity is not established.

Appendix D.7 approximates the foreign-key win probability by matching distributional endpoints and introducing an additive exponential-noise model. The construction gives a plausible interpolation, but matching the endpoints does not determine the distribution between them. The derivation also introduces an angle-sufficient factorization assumption that reduces interactions among class-specific carrier sets to a single comparison angle. It is not clear when the angle adequately summarizes the joint ranking behavior of the Fisher-combined scores.

Table 9 illustrates why the scope matters. For the tuned Amazon-Ratings configuration, the raw Corollary 2 approximation predicts an attribution success probability of approximately 4×10−54\times10^{-5}, while the measured OAA is 96%. The configuration uses 5,000 watermarked nodes, exceeds the main utility budget, and does not satisfy the stated 95% detection condition. The discrepancy therefore falls outside the stated high-confidence regime. The appendix reports the discrepancy and introduces an empirical calibration, but the practical range of the original formula still needs to be stated clearly. The empirical calibration should also be distinguished from the original theoretical approximation.

At a fixed watermark configuration, let P‾⋆>0\overline P^\star>0 denote the average probability that one foreign key beats the true key, and let BB denote the number of buyers. The factor (1−P‾⋆)B−1(1-\overline P^\star)^{B-1} then tends to zero as the buyer count BB grows. The wording that the attribution rate "saturates" needs a clearer interpretation. The empirical scalability evidence extends to 1,000 buyers; larger capacity estimates should be presented as conditional predictions of the approximation, with its assumptions and accuracy made explicit.

4. The trigger-based baseline detection comparison does not use matched false-positive budgets.

Appendix C.2.3 applies a Bonferroni-corrected threshold to the proposed method, but trigger-based baselines are declared positive when their verification success rate exceeds 1/C1/C, where CC is the number of classes. Exceeding chance prediction accuracy is not equivalent to passing a calibrated statistical significance test. In particular, when detection fires if any of 1,000 buyer probes crosses the threshold, the probability of a benign suspect triggering at least one probe can be substantial.

Appendix H.1 explains that the chosen rule causes benign models to trigger on at least one of the 1,000 buyer probes. Consequently, the poor detection accuracy of the trigger baselines partly reflects the thresholding protocol. The results do not isolate the methods' detection performance at a common false-positive operating point.

I would like to see the methods calibrated on separate benign suspects to the same familywise false-positive rate across the buyer pool, followed by a comparison of detection power and attribution accuracy. Reporting detection performance across multiple calibrated operating points would also help. Such calibration may not resolve the poor buyer ranking or cross-trigger interference of the baselines, but it is needed to assess the detection advantage fairly.

Questions for authors

Q1. Can Eq. (31) be corrected using the actual Fisher survival function, and can the authors provide a valid finite-sample statement replacing Corollary 1? How are the Fisher-combination correction, the required tail assumptions, and the uncertainty in variance estimation handled?

Q2. How is false-positive control established for the complete black-box selection-and-distillation procedure, including the benign fallback and selection errors? Under Eq. (5), how should the 28% empirical false-positive rate implied by Table 22 be reconciled with the claimed 5% level? Can the authors confirm that the reported black-box results use the corrected threshold stated in Appendix C.3?

Q3. What assumptions justify reducing the interactions among class-specific watermark carriers to a single-angle attribution model? Over what range of class counts, effective ranks, and buyer counts does the approximation remain accurate without empirical recalibration?

Q4. How do detection and attribution compare when all methods are calibrated to the same familywise false-positive rate over 1000 buyers?

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Paper summary

The paper proposes a radioactive watermark for node-classification datasets assigned to multiple buyers, aiming to verify whether a suspect GNN model is trained on benign data or leaked data from a buyer. Each buyer's copy is perturbed in the features of a small subset of nodes with a unique private key. After training on the perturbed nodes, the GNN surrogate model's embedding shifts align with buyer-specific per-class random directions. The detection is architecture-agnostic and supports both balck-box and white-box threat models.

Critical strengths
  1. Relevant problem and clear motivation. Buyer-level attribution from the trained model alone is the right target for enforcing restricted-use licences in data marketplaces.

  2. Statistically grounded detection with a broad evaluation. Detection returns a p-value under an explicit null with Bonferroni correction over BB keys, which is more defensible as evidence than threshold-based verification success rates. The evaluation covers eight GNN architectures, five graph datasets with various sizes and homophily levels.

Critical weaknesses
  1. Buyer attribution is not established under the stated threat model.

(a) Collusion is not evaluated: buyers with differently watermarked copies can differ them to locate the watermark nodes, then remove them. Buyers could also average or mix their copies. Collusion resistance is a defining requirement of buyer-traceable fingerprinting (Boneh & Shaw, 1998). While the paper cites this work, it does not evaluate collusion attacks.

(b) In the black-box setting, Stage 1 picks the buyer by loss gap on VwV_w (ad hoc threshold τd=0.5\tau_d=0.5), and the student is distilled only on that buyer's copy, so attribution may come from this membership-style signal rather than the radioactive test. Also here, related work on membership inference on GNNs is missing.

(c) The baseline comparison at B=1000B=1000 is not fairly calibrated. Trigger baselines declare detection if the maximum VSR across 1,000 probes exceeds 1/C1/C, without correcting for multiple testing. Moreover, per-buyer Backdoor triggers differ only in a scalar value encoded in the same 20 dimensions. The reported advantage over these baselines therefore partly reflects the evaluation protocol rather than the effectiveness of the proposed method.

  1. Limited novelty relative to Radioactive Data, and overstated theoretical guarantees. The core mechanism closely follows Sablayrolles et al., (2020), i.e., random per-class carriers, perturbations optimised against a fixed surrogate, cosine similarities between carriers and classifier weights, a Beta-distributed null model for cosine similarities, Fisher combination, and linear alignment between the marking and suspect feature spaces. However, the paper does not compare against a direct adaptation of Radioactive Data. Also, the theoretical guarantees seem overstated:

(a) Corollary 1 does not provide a certificate from design parameters alone. Although claimed otherwise, μ\mu and σ^\hat{\sigma} are estimated using calibration suspects trained on DwmD_{wm}.

(b) The derivation relies on questionable statistical assumptions. It sets Var(sc)=1/keff\mathrm{Var}(s_c)=1/k_{\mathrm{eff}} under H1H_1, effectively using the null variance, and asserts E[RFisher]=−C/2\mathbb{E}[R_{\mathrm{Fisher}}]=-C/2, exactly cancelling the C/2C/2 term.

(c) Assumption 1 is violated by the paper's own experiments. The assumption keff≤Ck_{\mathrm{eff}}\le C does not hold for the reported values in Table 5 (keff=46,80k_{\mathrm{eff}}=46,80) and Table 7 (46,6346,63), where C=40C=40.

(d) Corollary 2 is empirically uninformative on Amazon-Ratings. It predicts an OAA of 4×10−54\times10^{-5}, whereas the empirical OAA is 96%, indicating a substantial mismatch between the theoretical bound and observed performance.

Questions for authors

Clarifications:

  1. Is VwV_w shared across buyers or resampled per buyer? How does attribution hold up when 2–5 colluding buyers differ, average, or mix their copies, and is at least one colluder still identified?
  2. Black-box setting: what is the attribution accuracy of Stage 1 alone, and of the full pipeline when Stage 1 is replaced by a random candidate? Is the Stage-2 cosine test run over all BB keys or only over i^\hat{i}? How was τd=0.5\tau_d=0.5 chosen, and what is its false-positive rate on benign suspects?
  3. How is a leaked model distinguished from a buyer's own licensed model?
  4. Which layer defines HθH_\theta and WcW_c for each suspect? For a 2-layer GCN the last layer is A^HW\hat{A}HW; for APPNP, GCNII and Graph Transformer the head is not a linear map on a fixed embedding. The alignment Xalign=Hs†HθX_{\mathrm{align}}=H_s^\dagger H_\theta depends on this choice.
  5. LHL_H penalises only the shift orthogonal to ucu_c, and Table 21 shows λ2\lambda_2 has no measurable effect. What bounds the parallel shift and protects predictions?
  6. Are the nodes in VwV_w drawn from the training split? H^\hat{H} is negative on almost every dataset, i.e., the watermarked model classifies VwV_w better than the benign model, which suggests the carrier acts as a label-correlated shortcut feature. Please also report ΔAcc\Delta\mathrm{Acc} per cell in Table 1 and accuracy on the kk-hop neighbourhood of VwV_w.

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