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Under review as a conference paper at ICLR 2027

Pathway-Aligned Supervision: Assigning Negative Samplers in Temporal Link Prediction

Abstract

Temporal link predictors combine node context with pair history, yet their scoring pathways usually learn from the same negative examples. A comparison that distinguishes node representations can provide no direct gradient to an independently parameterized, deterministic history residual: identical history inputs cancel that residual in a pairwise score difference. This mismatch motivates Pathway-Aligned Supervision (PAS), which assigns random negatives to the node-score loss and historical negatives, with random fallback, to the full pair-score loss. With the scoring architecture fixed, we compare all four assignments and a validation-selected shared mixture. On tgbl-review, PAS raises the test mean reciprocal rank of a TGAT-based predictor from 0.20 under all-random supervision to 0.49 and exceeds the selected mixture; disjoint seeds confirm the gain. Better training contrast does not guarantee better ranking, however: PAS hurts tgbl-wiki, and changing evaluation candidates can reverse its advantage without retraining. Component experiments reveal a further distinction: a fitted history residual can help ranking even when changing its negative supervision harms the complete predictor. These findings support assigning negatives at the component level while evaluating the assignment under the intended ranking task.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Temporal link prediction, Negative sampling, Pathway-aligned supervision, Candidate-set sensitivity

Reviews

Among:
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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_BaV4OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

This paper focuses on the problem of negative sampling during training for dynamic/temporal link prediction. The author's thesis is twofold: (a) historical negatives should be used during training in addition to random negatives; (b) the type of negatives should differ for different model components. Based on this, the authors design a new training method that uses two different losses to update a node and pairwise scorer with a shared encoder. They further employ a mixture-based method that mixes the losses for both scorers. They test their method on two datasets, detailing the results.

Critical strengths
  1. The performance improvement on tgbl-review is good.
Critical weaknesses
  1. The paper writing is extremely unclear. To be blunt, I had a very time reading and understanding this paper. I include some concerns below from the first two sections:
    (a) What's sN=gnodes_N = g_{\text{node}} and sP=gpair=hreprs_P = g_{\text{pair}} = h_{\text{repr}} on line 109 mean? sNs_N, gnodeg_{\text{node}}, sPs_P, and gpairg_{\text{pair}} have never been introduced.
    (b) What's the point of having hreprh_{\text{repr}} is those representations are already passed to hnodeh_{\text{node}}? It's not explained.
    (c) What's xpx_p on line 115? Where is it used? Why is it defined as such?
    (d) It would be much easier if you concretely defined RR and HH in terms of equations. Because it's really hard to understand the authors based on their writing alone.
    (e) Why is λ=0.25\lambda=0.25 in Eq. 3?
    (f) Why do the RR negatives only update the hreprh_{\text{repr}} loss and HH for hnodeh_{\text{node}}? It's not explained.
    (g) What's "XY" on line 148?
    (h) I'm unsure what's happening in section 2.3. I thought that the HH and RR negatives are only applied to specified model components? Why are they being mixed now?

  2. Is evaluation unchanged? Specifically the negatives? One thing I'm concerned about is that some historical negatives used during training bleed into evaluation. It's unclear to me is that's controlled for.

  3. The loss analysis (Section 3) is confined to xpx_p. However, the score f(s,d)f(s, d) contains other components as well (on line 196 this is called grestg_{\text{rest}} which I assume is both hreprh_{\text{repr}} and hnodeh_{\text{node}}). So yes, they would have the same fixed history encoding, but we will still have the learnt encodings! These will very likely be different. If anything, this is just a limitation of the encoding. So in practice, I'm unsure how much this actually matters.

  4. So from my understanding RRRR is the standard training protocol (please correct me if I'm wrong). If that's true, it's seems that the it actually does quite well on tgbl−wikitgbl-wiki. So it seems that this strategy only helps sometimes? When is this the case and why? It's unclear.

  1. The authors only use 2/5 of the link prediction datasets in the TGB benchmark. Why? This severely limits the analysis and results because we have no idea what happens on those other datasets.

  2. Section 5 essentially just references the appendix. However, the experiments in the main text should be ``self-contained'' as per the author guidelines. This further reduces the readability of the paper.

  3. The authors should use newer and better temporal methods. Some examples include [1, 2] which do better than the methods used by the authors. It's unclear what the results will be on these methods than those used by the authors.

Questions for authors
  1. All my comments in weakness 1.
  2. Is the evaluation the same as used in the original TGB paper? (weakness 2)
  3. Why does the H loss help sometimes but not other times? (weakness 4)
Reviewer_9JJvOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper showed that, in temporal link prediction, predicting a link to a node with no prior interaction is harder than predicting a link to those with prior interactions, not just because it is hard by nature but in part because of the way in which we train the link prediction method. Specifically, in contrastive learning for temporal link prediction, a link prediction model learns a novel link between a node qq (query) and another node pp (positive) with no prior interaction, as well as a non-link between query qq and a randomly sampled negative node, nn. Since the negative node nn often does not have prior interaction with qq (due to the sparsity of many real-world networks), both positive pp and negative nn do not provide information on when query qq is linked with positive pp but not with negative nn through historical data. Only node-specific features can be used to make a prediction for a novel link, limiting the model's prediction capability.
To address this problem, the paper introduced a new negative sampling method, where the negative node nn is sampled from the set of nodes that have prior interaction with query qq. This encourages the model to learn the first-time link effectively. Tested on three datasets using a specific set of pairwise node features, the authors demonstrated that for one benchmark, the proposed method improves the link prediction accuracy by a large margin.

Critical strengths

Decomposing a link prediction problem as a composite of two objective functions, dedicated to learning node features and pairwise node features, motivated by the observation that most training data do not contribute to learning a novel link, is novel, and I find it very interesting.

Moreover, the paper showed that simply sampling historical negatives (nodes that have prior interaction with the query node) is not sufficient. The paper showed that it is crucial to separate the two components, each trained on different training data (one for node-pair representation learned through historical negatives, and another for node-specific representation learned through negatives sampled uniformly at random). This architecture, motivated by the training data distribution, would be transferable and may open up new model architectures and training frameworks.

Critical weaknesses
  1. A weakness of the paper is the lack of justification for the narrowed definition of "historical" data. The authors consider two components; one is about node-specific features. The other is about historical features for two nodes. The authors narrowly define "historical feature" as a few summary statistics, such as the frequency and recency of prior interactions. And based on this set of variables, the proof shows that nodes with no prior interactions do not contribute to learning the likelihood of novel links. I'd argue that the theoretical justification is very limited, as it assumes the features are author-selected variables. There are many kinds of pairwise features (e.g., graph structure). One can form pairwise node features from node features that encode the "historical" information (in fact, the authors included the historical information). This narrowly defined set of variables sets the boundary of the claim. I don't think narrowness is the only reason for rejection. However, because the entire research design and results hinge on selecting these variables, it is essential to explain why they should be considered and why the results generalize to broader settings.

  2. The general applicability is not demonstrated. While the issue addressed appears to be quite general, whether the fix improves the prediction or not depends on the dataset and how the evaluation set is formed. I appreciate the authors being transparent about that, which is very useful for knowing the boundary of the proposed solution. Yet, the paper can be improved to identify the condition in which the proposed solution leads to better outcome and that does not. The paper already showed an important contrast between tgbl-wiki and tgbl-review, and while the authors admitted that the cause is not clear, understanding the mechanism of when historical pairwise features provide useful insights to enhance the training framework and architecture design. Furthermore, it is crucial to show the effectiveness of the proposed solutions for a broader range of datasets.

  3. The presentation of the paper can be significantly improved. There are many notations that are not defined before they are used. For example, xex_e, xp(s,d,t)x_p(s,d,t). The definition of xex_e and xpx_p are presented in a later page of the main text or SI. Some notations are lightly explained such as grestg_rest (the first term contains all other components), cpairc_pair "log pair count". These undefined variables prevent the reader from understanding the main text. Furthermore, each form of the feature such as log⁡(1+...)\log (1+...) is not explained. No explanation for the recency for unseen pair to be -1.

Questions for authors
  1. Why should we focus on the pariwise node features selected? Why not other features? Are the node features that encode historical data historical features?

  2. Why did the proposed remedy improve or degenerate the performance of link prediction for wiki and review datasets? What are the mechanism that explain this? If the mechanism is identified, does this explain whether the method improves or degenerate the link prediction accuracy for broad range of datasets?

  3. Are the equations and derivations understandable for readers when the definition of the notations is not presented? What would be the least mentally-demanding ways to explain and use the notations?

Reviewer_jt7pOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies negative sampling for temporal link prediction. The predictor adds a node score and a pair score. The pair score includes a small history residual built on three pair features: pair count, a seen-pair indicator, and pair recency. Proposition 1 shows that this residual gets no gradient under a pairwise-difference loss when both candidates have the same residual inputs. The main example is two pairs that have never been seen.

The proposed method, Pathway-Aligned Supervision (PAS), trains the node loss on random negatives and the pair loss on historical negatives, with a random fallback. The authors cross the two samplers with the two losses (RR, RH, HR, HH). They also add a shared mixture selected on validation data. TGAT is the main encoder, and TCL is a second encoder. Training uses a strict timestamp-group history rule and a fixed budget of three epochs.

On tgbl-review, RH reaches 0.4855 test MRR, compared with 0.2046 for RR. RH beats the selected mixture by 0.0477 on the development seeds and by 0.0541 on the held-out seeds 45 to 49. On tgbl-wiki, RH is worse than RR (−0.0655). On tgbl-comment, RH gains 0.2598 with the official candidates. However, it loses 0.0472 when the same checkpoints are scored on uniform candidates. On review, the gain drops to 0.0016 with uniform candidates. Component retraining and residual removal at fixed checkpoints show that the review effect comes from the history residual. A long appendix adds older probes, residual-expert variants, and benchmark tables under other protocols.

I see the main contribution as a careful factorial study. It shows that assigning samplers per component can matter. It also shows that this benefit depends strongly on the dataset and on the evaluation candidates.

Critical strengths
  1. The core experiment is well controlled and honestly reported. The architecture, loss weight, and training budget are the same across all four assignments (Section 4.1). The shared mixture is chosen on validation data. Seeds 45 to 49 were run only after the comparator was fixed (Appendix B.7). The supplement links its summaries to file hashes, and its verify_release.py script runs cleanly and reproduces the Table 1 counts. The authors also report the unfavorable wiki and comment results in the main text. This makes the positive review result credible within the stated protocol.

  2. The fixed-checkpoint candidate replay is a valuable result in its own right. Scoring the same checkpoints on uniform candidates reverses the comment effect and almost removes the review effect (Table 4). The residual-removal analysis then locates the effect in the history residual (Table 5B). This is an important lesson for the field. Conclusions about samplers drawn from the official TGB candidate sets may not carry over to other candidate sets.

Critical weaknesses
  1. The headline gain is measured against a weak baseline, and it depends on the evaluation candidates. The abstract reports an MRR increase from 0.20 to 0.49 on review. Table 1 shows that under random negatives, both candidates are novel on 99.80% of review training queries. So in the RR setting, the history residual can get a direct gradient on at most 0.20% of queries. It is still added at full weight at test time, and it lowers RR's MRR by 0.1272 (Table 5B). Without the residual, RR and RH score about 0.332 and 0.335 (Section 4.5). In other words, about 0.13 of the 0.28 gain comes from removing harm caused by a component that RR can barely train. RR's score of 0.2046 is also below the published TGAT result on review (0.355 ± 0.012, Table 38), although the protocols differ.

Against stronger comparisons, the effect is smaller. RH beats the selected mixture by 0.0477 ± 0.0252 over three development seeds. My two-sided 95% t-interval for this margin is roughly [−0.015, +0.110]. The confirmation margin of 0.0541 is more convincing. Still, the review gain falls to 0.0016 with uniform candidates (Table 4B), and the comment result reverses (−0.0472). By the paper’s own count, strictly historical destinations fill 7.86 of every 100 official negatives on review and 32.17% of official slots on comment, compared with 0.0043 per 100 and 0.114% under uniform candidates (Section 4.4). PAS trains the pair path on this kind of negative. The paper notes that its design does not isolate the cause. Even so, the pattern fits the idea that PAS learns the makeup of the official candidate sets. This limits how much the main claim matters in practice.

  1. The supported contribution is narrow, and the extra material makes it hard to find. The strict positive evidence covers two encoders on review (TGAT and TCL) and TGAT alone on comment, under official candidates. The wiki result goes the other way. Proposition 1 is a simple identity: the same inputs to one function cancel in a difference. Proposition 2 is a standard Lipschitz bound. As Section 3 acknowledges, neither one predicts when the assignment will help ranking.

Appendices C to G add more than 30 pages that do not meet the paper's own strict standard. The older record-order rule used same-timestamp events on 100% of sampled review queries (Appendix B.2). Several tables have run mappings that can no longer be recovered. Examples are the TPNet+PAS cells for comment, coin, and flight (Appendix E.8) and DTLP-node (Appendix F.5). Other results do not state what was repeated (Figures 6 and 18; Tables 15 and 16). Table 38 still lists TPNet+PAS values, such as 0.945 on comment, next to leaderboard entries. Readers could easily take these as benchmark claims. The large amount of qualified, non-comparable material makes the paper hard to evaluate.

Questions for authors

Q1. Could you report two all-random baselines under the strict protocol? The first would drop the history residual in both training and inference. The second would use the standard TGAT link head. How large is the RH gain against these baselines on review, wiki, and comment?

Q2. Both candidates are novel on 99.80% of review training queries (Table 1). Would a simple one-parameter rule match RH on the official candidates? One example is RR plus a validation-tuned penalty on the seen-pair indicator. If it does, what does the learned residual add beyond the sign of that penalty?

Q3. The shared-mixture grid is ω ∈ {0, 0.25, 0.5, 0.75, 1}. Review test MRR goes from 0.2046 at ω = 0 to 0.4378 at ω = 0.25, then down to 0.3195 at ω = 0.5 (Appendix B.6). Would a finer grid, such as ω ∈ {0.1, 0.15, 0.2, 0.3}, reduce the RH margin?

Q4. In the sealed TCL summary, all four wiki arms for seed 42 score between 0.06 and 0.11. Seeds 43 and 44 score between 0.53 and 0.67. Did the seed 42 run fail? The per-seed TCL wiki RH − RR values are +0.012, −0.127, and −0.090. If seed 42 failed, the claim of "the same mean directions" (Section 5.1) would rest on only two seeds.

Q5. The training budget is three epochs (Appendix B.6). In the multi-negative and comment summaries, 22 of the 60 selected checkpoints come from the last epoch. On wiki, 11 of the 12 RR and RH checkpoints in the multi-negative cohort come from epoch 1. Does the ranking of the four assignments hold with a longer budget and early stopping?

Suggestions:

S1. Please report the uniform-candidate replay for all four arms on review and wiki, not only for RR and RH on review. It would also help to state in the abstract that the review gain nearly disappears with uniform candidates.

S2. Please consider moving the older DTLP, PDRE, TPNet+PAS, and CRAFT material to a separate archive, or removing rows whose run mapping cannot be recovered. Table 38 in particular should not mix these rows with leaderboard entries.

S3. The supplement does not include data, checkpoints, or per-query ranks, and verify_release.py checks only Table 1 from aggregate numbers. Releasing per-query ranks for Tables 2, 4, and 5 would let readers verify the main effects.

Comments about references: Chen et al. (2024) is cited as arXiv:2407.17070. It has since been published in Neural Networks, vol. 191, article 107858 (2025). Yi et al. (2025a) could add pages={2347--2375} "Yi, L., Lei, R., Mo, F., Zheng, Y., Wei, Z., & Ye, Y. (2025). Future Link Prediction Without Memory or Aggregation. Advances in Neural Information Processing Systems, 38, 2347-2375." Please check your references to have the page numbers as well.

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

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