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Paper summary
This paper presents GO-Flow, a positive-only graph learning framework for predicting unobserved relations and identifying candidate nodes. Motivated by the fact that missing edges or unlabeled nodes are not necessarily negative examples, GO-Flow trains a conditional flow using observed positives alone. For relation prediction, it scores candidate pairs by comparing the conditional likelihood of a target under its graph context with its likelihood under a background context. The method also supports a positive-only structural encoding to complement the flow-based score. A theoretical analysis connects the proposed density contrast to optimal ranking under specific assumptions. Experiments cover link prediction, drug–target interaction, and node ranking, with additional studies on false-negative contamination, model selection, alternative estimators, and computational efficiency.
Critical strengths
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I find the motivation both practical and well grounded. In applications such as drug–target interaction prediction, an unobserved relation may simply not have been discovered, so treating every missing edge as a negative example can introduce misleading supervision. GO-Flow addresses this issue by learning exclusively from confirmed positive relations and using graph-conditioned distributions to evaluate new candidates. What I particularly appreciate is that the authors clearly distinguish positive-only parameter training from model selection. This makes the scope of the proposed setting more transparent rather than presenting it as a completely negative-free pipeline.
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Another interesting contribution is the conditional-to-background density contrast. Instead of ranking a candidate solely by how likely its features are under the learned positive distribution, GO-Flow asks whether the corresponding graph context makes those features more plausible. This is a meaningful distinction, since common node features should not automatically imply a strong relation. The results in Table 6 provide direct evidence for this design, with the background contrast improving over conditional likelihood alone across the five evaluated datasets. I also appreciate the analysis in Section 4.4 showing that a better fit to the positive distribution does not necessarily produce better rankings. This observation gives the scoring mechanism a clearer justification beyond simply applying Flow Matching to graph data.
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I particularly appreciate the effort to examine the method's limitations rather than focusing only on favorable comparisons. GO-Flow performs strongly against positive-only baselines across the link-prediction benchmarks and shows encouraging results on drug–target interaction tasks. Beyond these results, the authors evaluate false-negative contamination, hard-negative ranking, direct density-ratio estimators, and positive-only model selection. Several of these experiments reveal situations where other methods perform better or where GO-Flow becomes less effective. Reporting these findings makes the empirical analysis more credible and helps readers understand the actual trade-offs of positive-only learning. The extensive supplementary experiments are also useful for identifying when the approach is most likely to work well.
Critical weaknesses
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I would like a clearer discussion of how much the reported performance depends on negative examples during model selection. Although GO-Flow trains its parameters exclusively on observed positives, its main evaluation protocol still uses sampled validation non-edges to select the encoder, conditioning strategy, scoring weights, and other configurations. I appreciate that the authors openly acknowledge this distinction and even investigate positive-only model selection in Appendix T. However, the reported average ROC-AUC drops by 0.049 when positive-only validation is used with structural encoding, with a particularly large decrease on PPI. This suggests that validation information plays a meaningful role in achieving the reported results. I do not consider this a contradiction of the positive-only training claim, but it does limit the method's applicability when reliable negative examples are unavailable throughout the entire pipeline. A more prominent discussion of this limitation, together with practical guidance on model selection in such settings, would strengthen the paper.
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The drug–target interaction evaluation protocol deserves further attention. Appendix J.2 explains that model configurations are selected using validation interactions drawn from the full interaction set, some of which later appear in the cross-validation test folds. Although the flow models themselves are not trained on these test interactions, their labels can still indirectly influence configuration selection. I appreciate the authors' transparency about this issue, but describing the resulting bias as small does not establish its actual magnitude. Since the DTI experiments provide some of the strongest results in the paper, I think an additional evaluation with strictly separated validation and test interactions would be valuable. For example, selecting configurations within the training portion of each fold would help determine whether the reported improvements remain consistent. This would also make the comparison with previously published PU methods more convincing.
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I am still somewhat uncertain whether the additional complexity of conditional flow matching is always justified. The conditional-to-background contrast is a sensible scoring principle, but estimating density ratios does not necessarily require learning a full conditional flow. I appreciate that Appendix S includes direct bilinear and MLP estimators trained using positive relations alone. Interestingly, these simpler alternatives outperform the flow-based score on UMLS and WN18RR, while requiring substantially less time to rank candidates. The reported scoring speed difference exceeds two orders of magnitude. GO-Flow performs better on the remaining six datasets in that comparison, so I do see value in the proposed approach. Still, a clearer discussion of the accuracy–efficiency trade-off would help explain when the flow model is worth its computational cost. I would also encourage the authors to distinguish the theoretical interpretation of the density contrast from a general ranking guarantee, since Proposition 1 relies on a specific independence assumption for non-relations.
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Some aspects of the evaluation could better reflect the challenges of real-world link discovery. In particular, the positive-only structural encoding includes endpoint degrees and path-based statistics, while conventional link-prediction benchmarks with randomly sampled non-edges can favor methods that exploit degree information. This issue is discussed in Implicit Degree Bias in the Link Prediction Task (Aiyappa et al., ICML 2025, https://proceedings.mlr.press/v267/aiyappa25a.html) and Bias-aware Training and Evaluation of Link Prediction Algorithms in Network Biology (Yılmaz et al., PNAS 2025, https://doi.org/10.1073/pnas.2416646122). I think these studies are particularly relevant given the biomedical applications considered here. The authors already provide HeaRT hard-negative results, which I appreciate, but GO-Flow is noticeably weaker than several negative-trained methods in that setting. Another issue is the difference between training and evaluation graph contexts. As discussed in Appendix C, training target edges remain available during message passing, whereas evaluated edges are excluded. The authors investigate target-edge masking, but its effect varies across datasets and configurations. A clearer interpretation of these findings, together with a degree-aware evaluation or additional analysis using existing results, would help establish how reliably GO-Flow identifies genuinely difficult and previously unseen relations.
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I think the presentation could better reflect the amount of experimental work that has been done. Figure 1 provides a useful conceptual overview, but it is quite simplified and does not fully explain how the graph encoder, conditional flow, background density estimation, and positive-only structural encoding fit together. A more complete architecture diagram would make the proposed framework easier to understand without requiring readers to reconstruct the workflow from the equations. I also noticed that almost all experimental findings are presented in tables, with very little visual analysis. This makes the paper feel somewhat dense despite the considerable amount of evaluation. Several existing results would be particularly suitable for visualization, such as performance changes under false-negative contamination, the relationship between positive-density quality and ranking performance, and the accuracy–efficiency trade-off against direct density-ratio estimators. A few carefully selected plots could make these findings much more intuitive. I do not think additional experiments are necessarily required here. Better organization and visualization of the existing evidence would already improve the paper substantially.
Questions for authors
Please see Weaknesses 1–4 above. I would particularly appreciate clarification on how much the DTI results are affected by the overlap between validation and cross-validation test interactions, and whether the main improvements remain consistent under a strictly separated evaluation protocol. I would also be interested in a clearer explanation of when conditional flow matching offers sufficient benefits over simpler density-ratio estimators to justify its additional computational cost. Finally, the limitations of positive-only model selection and the generalization to more challenging candidate relations deserve further discussion.
4 comments
Authors Responses (Part 2)
Regarding a strictly separated protocol for drug–target interaction (W2, Q). Thank you for proposing a strictly separated evaluation. As you suggested, we selected configurations within the training portion of each fold: inside every one of the 50 cross-validation folds (150 per family over three seeds), on 15% of the training interactions of that fold, with ten non-interactions each drawn from pairs that are not test candidates of the fold. No test pair, positive or negative, informs any choice (Tables 2 and 13):
| ROC-AUC | Enzyme | Ion channel | GPCR | Nuclear receptor |
|---|---|---|---|---|
| Strongest positive-only baseline (Table 2) | 0.798 | 0.825 | 0.790 | 0.739 |
| PUDTI [3] (as published) | 0.898 | 0.875 | 0.894 | 0.907 |
| PUDT-Lan [4] (as published) | 0.884 | 0.831 | 0.878 | 0.885 |
| GO-Flow, submitted protocol (Table 2) | 0.968 | 0.969 | 0.956 | 0.894 |
| GO-Flow, nested selection | 0.963 | 0.966 | 0.954 | 0.854 |
Under nested selection, GO-Flow reaches 0.963, 0.966 and 0.954 on Enzyme, Ion channel and GPCR, within 0.005 of the submitted protocol and 0.060–0.091 above every published positive–unlabeled (PU) method. On Nuclear receptor, the smallest family (90 interactions, about 11 validation positives per inner split), it reaches 0.854, below PUDTI and PUDT-Lan. On all four families it remains 0.115–0.165 above the strongest positive-only baseline. In the revision, Appendix J reports the nested protocol beside the submitted one, Tables 2 and 13 add the nested rows, and Appendix K adds nested ranking metrics.
Regarding the cost of the flow and the role of the theory (W3, Q). Thank you for asking when the flow is worth its cost. Table 24 (Table 22 in the original submission) compares the flow score with the bilinear and MLP estimators of Appendix S, which estimate the full contrast (w = 1) by classification:
| ROC-AUC | Cora | CiteSeer | UMLS | WN18RR | DISEASES | Drug–Disease | PPI | Ohmnet |
|---|---|---|---|---|---|---|---|---|
| Bilinear | 0.817 | 0.805 | 0.985 | 0.671 | 0.678 | 0.632 | 0.676 | 0.617 |
| MLP | 0.811 | 0.918 | 0.974 | 0.715 | 0.782 | 0.628 | 0.711 | 0.635 |
| GO-Flow without the PSE (α = 0) | 0.913 | 0.935 | 0.911 | 0.656 | 0.920 | 0.639 | 0.829 | 0.746 |
The flow score is higher on six of the eight graphs, by 0.11–0.14 on DISEASES, PPI and Ohmnet, and the direct estimators are higher on UMLS and WN18RR; they score 100,000 candidates in 0.03–0.07 s, compared with 9.68 s. The flow is worth its cost where the direct estimators are behind on validation; where a direct estimator matches the flow on validation, it is the better choice. Five integration steps instead of twenty run 3.3–4.0× faster for a median ROC-AUC decrease of 0.007 (Appendix Y). Following your suggestion, Section 4.4 now discusses this trade-off with Figure 5. On the theory, Proposition 1 states optimality under a model of non-relations, and w is selected because that model is unknown. In the revision, Section 3.2 presents Proposition 1 as an explanation of the score under this model, and Appendix B distinguishes this theoretical interpretation from a general ranking guarantee.
Authors Responses (Part 3)
Regarding degree-aware evaluation and difficult relations (W4, Q). We appreciate the references and the question on how reliably GO-Flow identifies difficult relations. As you suggested, we added a degree-aware evaluation on all eight link datasets with the splits, configurations and seeds of the paper: degree-corrected non-edges, with endpoints drawn in proportion to their training degree [1, 2], degree-matched non-edges in the same log2-degree bins as each positive, and ROC-AUC stratified by degree. SEAL, BUDDY, NCNC and LPFormer are scored on the same negatives of the six graphs of Table 4 (Appendix Z, Tables 31 to 33). The evaluation complements the HeaRT evaluation of Section 4.3 [5], where negatives are chosen by heuristics to resemble true edges, which negative-trained methods can learn to reject:
| ROC-AUC, degree-corrected non-edges | Cora | CiteSeer | UMLS | WN18RR | PPI | Ohmnet |
|---|---|---|---|---|---|---|
| SEAL | 0.836 | 0.835 | 0.972 | 0.870 | 0.634 | 0.731 |
| BUDDY | 0.885 | 0.922 | 0.975 | 0.686 | 0.575 | 0.706 |
| NCNC | 0.936 | 0.949 | 0.938 | 0.762 | 0.601 | 0.715 |
| LPFormer | 0.888 | 0.917 | 0.946 | 0.752 | 0.612 | 0.730 |
| GO-Flow without the PSE (α = 0) | 0.867 | 0.903 | 0.840 | 0.630 | 0.505 | 0.535 |
| GO-Flow with the PSE | 0.849 | 0.849 | 0.877 | 0.571 | 0.546 | 0.621 |
On Cora, CiteSeer and UMLS, the four negative-trained methods decrease by 0.01–0.06 from Table 4 under degree correction, about as much as the flow (0.03–0.07), while PSE-only reaches 0.540 on Cora and 0.459 on CiteSeer; on the lowest-degree tertile of Cora positives and the standard non-edges, the flow reaches 0.831, compared with 0.408 for PSE-only. On WN18RR, PPI and Ohmnet, the negative-trained methods decrease by 0.06–0.29 and reach 0.57–0.87, and the flow reaches 0.505–0.630. On the four drug–target families, we scored the configurations selected in every fold of the nested protocol on degree-corrected non-interactions (Table 33):
| ROC-AUC, GO-Flow under nested selection | Enzyme | Ion channel | GPCR | Nuclear receptor |
|---|---|---|---|---|
| Standard non-interactions | 0.963 | 0.966 | 0.954 | 0.854 |
| Degree-corrected non-interactions | 0.945 | 0.943 | 0.899 | 0.811 |
The drug–target results therefore decrease by 0.018–0.055 under degree correction; with the flow without the PSE, Nuclear receptor reaches 0.839, while PSE-only reaches 0.296–0.562 and the weighted-profile baseline reaches 0.578–0.650 (Table 33). Appendix Z of the revision reports this evaluation.
Regarding training and evaluation contexts (W4). Thank you also for asking how to read the masking study of Appendix C. Removing the target edges of each minibatch from message passing during training raises ROC-AUC on Cora and CiteSeer by 0.013 and 0.004 beyond random edge dropout, and on these graphs the flow does not depend on seeing the target edge; on PPI it lowers ROC-AUC by 0.082 beyond random dropout, and with the PSE the effect is within 0.021 of random dropout on all three graphs:
| Test ROC-AUC, configuration of Appendix C (Table 8) | Cora | CiteSeer | PPI |
|---|---|---|---|
| Without the PSE, unmasked | 0.917 | 0.925 | 0.642 |
| Without the PSE, random edge drop | 0.929 | 0.955 | 0.613 |
| Without the PSE, target edges masked | 0.942 | 0.959 | 0.530 |
| With the PSE (α = 0.5), unmasked | 0.855 | 0.798 | 0.812 |
| With the PSE (α = 0.5), random edge drop | 0.879 | 0.847 | 0.804 |
| With the PSE (α = 0.5), target edges masked | 0.884 | 0.833 | 0.783 |
Evaluated edges are never in the message-passing graph, and the reported numbers therefore assess unseen relations. Following your comment, Appendix C now gives this interpretation.
Authors Responses (Part 4)
Regarding figures of the existing evidence (W5). We are grateful for the suggestions on presentation. As you proposed, we added three figures from existing results: (i) ROC-AUC under contamination on Cora and retention on all five graphs (Figure 3); (ii) held-out log-likelihood and ROC-AUC for independent, optimal-transport and reflow couplings on the five graphs of Section 4.4, showing the two objectives moving in opposite directions on four of the five (Figure 4); (iii) ROC-AUC and scoring time of the direct estimators and of the flow at each integration budget (Figure 5). We also added an architecture diagram (Figure 2, Appendix C, referenced from Section 3) with a training panel and a scoring panel. It shows the encoder, the target–context construction under cross-endpoint and joint conditioning, the conditional and null contexts of the one velocity field, the change-of-variables log-density, the contrast, the node-pair score, and the rank fusion with the PSE; its caption names the equation of each stage.
We sincerely appreciate the constructive feedback, which strengthened both the evaluation and the presentation of our work. We hope that the nested protocol, the degree-aware evaluation, the model-selection measurements and the new figures address your concerns, and that you will consider revising your score. We are happy to discuss any remaining questions.
References:
[1] Implicit degree bias in the link prediction task
[2] Bias-aware training and evaluation of link prediction algorithms in network biology
[3] Screening drug-target interactions with positive-unlabeled learning
[4] Predicting drug–target interaction using positive-unlabeled learning
[5] Evaluating Graph Neural Networks for Link Prediction: Current Pitfalls and New Benchmarking
Authors Responses (Part 1)
Thank you for the thorough and constructive review, and for the references on degree bias [1, 2]. We are glad that you found the motivation "both practical and well grounded", appreciated that we "clearly distinguish positive-only parameter training from model selection", found that the conditional-to-background contrast draws "a meaningful distinction", and valued "the effort to examine the method's limitations". We hope that you find our responses satisfactory, and that you will consider revising your score.
In short: your review asks whether the reported results hold under stricter protocols and harder candidates, and how the existing evidence can be organized and visualized. Following it, we:
Regarding model selection and practical guidance (W1, Q). We appreciate the question on how much the reported performance depends on validation non-edges. We evaluated one configuration fixed in advance, the configuration of Appendix C (GCN, FiLM, cross-endpoint conditioning, the full contrast, no reflow, fusion weight α = 0.5 with the positive-only structural encoding, PSE), on all eight link datasets with no validation non-edge anywhere (Table 25):
It averages 0.819 ROC-AUC, compared with 0.880 with per-dataset selection and 0.768 for PSE-only, the strongest positive-only baseline of Table 1 on average. We also introduce a criterion built only from observed positives, the ROC-AUC with which validation positives rank above recombined validation positives. It selects every setting of the flow without the PSE, and its choice is 0.011 ROC-AUC below the choice made with validation non-edges on average (0.095 lower on PPI, where the positive-only criteria of Appendix T lose 0.264). With the validation non-edges contaminated at the training rate for GO-Flow, BUDDY and NCNC, GO-Flow retains at least 97% of its ROC-AUC at 40% contamination on all five graphs:
Following your comment, Sections 3.2 and 4.4 now state this dependence with practical guidance: without reliable validation negatives, use the fixed configuration, which needs no selection criterion and is 0.061 lower on average and 0.137 lower on CiteSeer; with a small set of trusted non-edges, select on them.