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Under review as a conference paper at ICLR 2027

Your Temporal Link Predictor Is Blind to Who Is Active: A Missing Factor That Transfers Across Models

Abstract

An interaction has two parts: someone decides to act, and then chooses whom to act on. Temporal link prediction has concentrated on the second, and we show that it is blind to the first by construction: a standard negative keeps the real source and swaps the destination, and we prove that this cancels the source's activity exactly from the optimal score, so no model trained and evaluated this way is ever rewarded for learning it. Under the harder historical and inductive negatives, whose sources differ, the same factor becomes the dominant signal. We model it with **Source Node Activity Modeling (SNAM)**, a self-exciting event intensity fitted by an exact point-process likelihood to decayed interaction counts the history states already contain; it has **fewer than 20 parameters**. On their own, never looking at the destination, **these parameters beat DyGFormer and TPNet** on four of five datasets under historical negatives. Added to the frozen scores of TPNet, TGN, DyGFormer and DSRD, four models of different design, **without retraining anything**, they raise AP on every backbone–dataset pair in both settings, by up to 25 points. Our full model ranks first overall against eleven baselines on 13 datasets and three protocols, and on million-event streams trains an epoch 9–100 times faster than TPNet and DyGFormer. We conclude that source activity is a blind spot of temporal link prediction, and a cheap, transferable one to close.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Temporal Graph Learning, Temporal Link Prediction, Multi-scale Temporal Representation, Event Intensity Modeling, Self-exciting Processes, Point Processes, Dynamic Graphs

Reviews

Among:
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1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.25 over 4 reviews, above 96% of the others.
Reviewer_LCktOpenReview ↗
Rating
4
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

The authors point out a crucial shortcoming in temporal link prediction: negative-sampling strategies for constructing training examples for current temporal-graph-learning models provide training examples that cancel out the course of interactions. Therefore, models become blind to which node is active, and they cannot use this information for making link predictions. To address this issue, the authors introduce SNAM (Source Node Activity Modeling), which I would paraphrase as "estimating nodes' activity at prediction time point t based on their recent history". A nice aspect of their approach is that it is extremely lightweight with "fewer than 20 parameters", and that it can be combined with TGNN models without the need for retraining. Across a range of standard temporal link-prediction benchmarks, the authors show the effectiveness of their approach and that it improves the performance of other TGNN models.

I find the paper very well written, and the authors' line of thought is easy to follow. There is a clear red thread through the paper, and nothing seems out of place. Personally, I would have preferred one page fewer of maths and definitions and instead some more figures and discussion that "looks under the hood" and helps the reader build intuition -- but that may just be personal preference.

Critical strengths

The authors present one simple idea that changes our understanding of how current TGNNs for temporal link prediction work and how the way we construct training data affects what they can learn.

Critical weaknesses

None

Questions for authors

I do have a couple of questions I have been thinking about while reading the paper:

  1. You mention in the second paragraph on page 2 that "SNAM [...] can be added to other link prediction models [...] without retraining". I understand this as "other models can use SNAM as they are, no retraining is necessary", but what if we decided to retrain? Is there some information that SNAM could provide during training that could improve performance even more? Don't get me wrong, I think it is a strength that no retraining is necessary. I am merely wondering about the "what if?".
  2. In the third paragraph on page 2, you mention that Multi-Timescale Historical Representation learns nodes' activity at K time scales. What are the breaking points of this approach? I suppose that it is difficult to detect every possible time scale at which a node might interact. For example, some nodes might interact at a high frequency while others interact infrequently. Yet others might have truly random interaction patterns so that they do not allow any sensible predictions. What happens, for example, when the data contains interactions at too many time scales, say 2K time scales? And are nodes that interact truly randomly somehow shoehorned into the K time scales?
  3. When reading the equations, it took a moment before I understood one detail of the notation: Take Eq. 9 where you write f(u,v,t)=max(z0,z1)f(u,v,t) = max(z_0,z_1). I did not immediately see where z0z_0 and z1z_1 came from, as they do not enter ff as a parameter. But then I realised that you probably used this as shorthand for the definition of zz from the line above, and then indexed it. Is that what you mean? This is probably not a huge problem, but the clarity might be improved a little here.
  4. The loss in Eq. 13 is a sum of two sub-losses, which makes me wonder whether there might be situations where one of them dominates the other. Specifically, could it be possible that the parameters are chosen in such a way that the "ordinary" link-prediction loss dominates the optimisation and the node-activity loss becomes negligible? Perhaps you have pointed this out somewhere, and I have missed this, but is there a property that guarantees "the same scale" for both losses or something similar that makes he composite loss well-behaved?
  5. What does the last row of Table 1 really show, that is, the row titled "Overall Avg. Rank"? Is it the average rank over three different negative-sampling strategies for all datasets? That is, does each dataset enter the number three times, once for each negative-sampling strategy? I am not entirely sure that this is a number that makes sense to calculate, as it somewhat mixes different things, but I may be wrong.

Minor points

  • The dagger symbol is used in Table 2, but only defined in Table 4.
  • What is the star in Table 3?
9 comments

Thank you very much for the careful reading and the kind, constructive questions!

Before the answers below, please read our two overall responses first, "Clarifying a Likely Misreading of Our Contribution" and "What Changed in the Revised Paper". They are important. They say what the paper claims and how the revised version is organized, and they may already answer many of the questions raised in the reviews. Our answers to your individual questions build on them.

AuthorsOpenReview ↗

Q1. What if the backbone were retrained together with SNAM?

Your reading is correct, and the "what if" has a definite answer. Retraining a model together with SNAM would give exactly the same model and exactly the same SNAM as training them separately, so there is nothing further to gain from it.

Take TPNet and suppose we retrain it together with SNAM. In every training step, TPNet's link-prediction loss is computed from TPNet's own scores. It contains neither SNAM's parameters nor SNAM's output. SNAM's loss is the likelihood of the event times, and it contains nothing from TPNet. Each step therefore changes TPNet's weights exactly as it would without SNAM, and changes SNAM's K+1K+1 parameters exactly as it would without TPNet. At the end we hold the same TPNet and the same SNAM as in Table 2, and adding them gives the same results.

In symbols, the joint objective is Eq. 13, L(Θ,ϑ)=Llink(Θ)+Lact(ϑ)\mathcal L(\Theta,\vartheta)=\mathcal L_{\mathrm{link}}(\Theta)+\mathcal L_{\mathrm{act}}(\vartheta), where Θ\Theta are the backbone's parameters and ϑ\vartheta are SNAM's. The two terms share no parameter, so the gradient of the sum with respect to Θ\Theta is the gradient of Llink\mathcal L_{\mathrm{link}} alone, and the gradient with respect to ϑ\vartheta is that of Lact\mathcal L_{\mathrm{act}} alone. Minimizing the sum is the same computation as minimizing each term by itself. When one minimizes (x−3)2+1000(y+1)2(x-3)^2+1000(y+1)^2 by gradient descent, the updates of xx do not depend on the second term, whatever its scale.

Training together gives a different result only when the two losses share parameters, as in multi-task learning, or when the output of one model enters the loss of the other. Neither holds here.

One could build such a coupling on purpose, for example by adding βlog⁡λu\beta\log\lambda_u to the backbone's score during training. By the analysis of Section 4.1 this would not help. A positive and its negative have the same source and timestamp under standard training, so the added term is the same for both, and the optimum of the trained score is the same as before. The backbone would only learn to offset the term. This is why SNAM is fitted on its own, by its likelihood, and added to the score after training.

AuthorsOpenReview ↗

Q2. Breaking points of the K timescales

We should have explained this in the main text. The KK timescales are not KK interaction frequencies that the model has to detect, and no node is assigned to one of them. They are KK fixed basis functions, and every node is described by all of them at once. The design follows from two mathematical facts, both in Appendix D.

Why exponentials. For each node uu and each decay rate ωk\omega_k we keep a decayed count of its past events,

nuk(t)=∑te<te−ωk(t−te),n_u^k(t)=\sum_{t_e<t}e^{-\omega_k(t-t_e)},

and the backbone keeps decayed sums of neighbour embeddings in the same way. The exponential is the only decaying weight for which such a sum can be updated exactly from its previous value, without going back through the history (Appendix D.1).

Why several, spaced logarithmically. A single exponential forgets at one fixed speed. Influence that fades slowly, such as a power law, is exactly a mixture of exponentials (Eq. D.5):

s−α=1Γ(α)∫0∞ωα−1e−ωsdω.s^{-\alpha}=\frac{1}{\Gamma(\alpha)}\int_0^\infty\omega^{\alpha-1}e^{-\omega s}d\omega .

Evaluating this integral at KK points equally spaced in log⁡ω\log\omega gives s−α≈∑k=1Kcke−ωkss^{-\alpha}\approx\sum_{k=1}^{K}c_k e^{-\omega_k s}, which is our grid (Appendix D.3). The KK rates are therefore the sample points of an integral, and the weights ckc_k are learned from the data. A pattern whose timescale lies between two grid points is represented by a combination of its neighbours, and a denser grid only makes the approximation finer.

The range of the grid comes from the data. Its fastest timescale is the smallest gap between two training timestamps, its slowest is the whole training period, and there are about two timescales per factor of ten in between, at most 16 in total (Appendix D.4). The fastest and the slowest behaviour in the training data are both inside this range.

With this picture, your questions have direct answers.

Data with 2K2K timescales. They do not have to coincide with ours, because any timescale inside the range is covered by the basis. We also ran this experiment. Doubling KK from our default (14 to 16) to 27 to 32 changes the transductive AP of our full model under historical negatives by at most 0.4 points on all five datasets, and costs about 1.3 times the training time (Tables 4 and 15, Appendix I.4). Two timescales per factor of ten are already enough.

Breaking point. Too few timescales. With K=1K=1 the same AP falls by 1.3 to 16.6 points, for example from 96.0 to 79.5 on UCI and from 90.2 to 77.5 on Reddit.

Nodes that interact truly at random. No. The model does not assign a node to a timescale, and every node, random or not, has all KK decayed counts. For a truly random node, whose events arrive at a constant rate, the times of its past events say nothing more about the next one, so the only thing that can be predicted is its average rate. The model has this rate. The slowest timescale spans the whole training period, so its decayed count is essentially the number of events the node has had, which is proportional to the average rate.

Reviewer_BLnHOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper argues that temporal link prediction should distinguish source activity from conditional destination preference. It shows that source–time factors cancel from the optimal discriminator under source- and timestamp-preserving negative sampling. To recover source activity, it proposes Source Node Activity Modeling (SNAM), which estimates a positive intensity from multi-timescale decayed interaction counts. SNAM is combined with cached historical aggregates and candidate-conditioned relation features to form the complete architecture for temporal link prediction. In addition, the SNAM module can be used as an add-on to existing methods for better performance without retraining them. Experiments on thirteen datasets are done to demonstrate the effectiveness of the proposed method.

Critical strengths
  1. The observation is interesting and useful. The source node activity state indeed needs to be modeled in temporal link prediction. The distinction between whether a source will act and whom it will interact with helps explain what conventional negative-sampling objectives actually supervise.

  2. The proposed modules are simple and effective. Comprehensive experiments have been done to evaluate the method, which cover 13 datasets and several evaluation settings. The proposed method improve substantially in both historical and inductive negative settings, which are considered to be more challenging than random negative setting. Testing the overall design and removing individual components also helps explain where the improvements come from.

  3. The results by adapting SNAM to four state-of-the-art models are convincing. The improvements shown have demonstrated the usefulness of source activity beyond the proposed relation encoder.

  4. The activity module is lightweight and operationally attractive. SNAM has only (K+1) shared parameters, reuses inexpensive historical statistics, and admits analytical integration in its training objective. Its simplicity makes the proposed correction practically interesting.

  5. The method offers practical benefits in addition to better prediction results. Reusing historical calculations makes training per epoch and prediction substantially faster on larger datasets. These efficiency gains make the approach appealing for processing long interaction streams.

Critical weaknesses
  1. It would be helpful to conduct experiments that can explicitly show how much of the improvement comes from distinguishing active sources from inactive ones by the proposed method.

  2. A complete architecture diagram may improve readability.

  3. It is better to have more illustrative examples in Section 4.1 and Section 4.2 as there are many technical terms and parameters here.

Questions for authors

Please refer to weaknesses.

5 comments

Thank you very much for your careful review and constructive comments!

Please read our two overall responses first, "Clarifying a Likely Misreading of Our Contribution" and "What Changed in the Revised Paper". All our answers rely on them. In short, SNAM is not a strong feature found to work on a benchmark. The version of the paper you reviewed made it look like one, which was the fault of our writing.

A model trained in the standard way scores which destination a source picks. The task, as the benchmark papers themselves state it, is whether a given pair interacts at a given time. Adding SNAM turns the score of any such model into a score for the stated task, without retraining it. In symbols, the trained score is log⁡π(v∣u,t)\log\pi(v\mid u,t), SNAM adds log⁡λu(t)\log\lambda_u(t) (how often the source acts), and the sum is log⁡λuv(t)\log\lambda_{uv}(t), the rate at which the pair interacts. The activity of the source is thus one of the two factors of the task, and it is the one that standard training leaves out. The gains under DyGLib's historical and inductive negatives are a consequence of this correction, not its target.

Following your comments on readability, we rewrote the main text. The diagnosis now opens the method section (Section 4.1), the engineering details of our backbone moved to the appendix, and Appendix A.1 gives the argument step by step. The method and the conclusions have not changed.

AuthorsOpenReview ↗

Q1. How much of the improvement comes from distinguishing active from inactive sources

Our argument rests on three facts that can each be checked, not on a definition of our own choosing (Section 4.1 and Appendix A.1 of the revised paper; our first overall response).

  1. Stated. The benchmark papers state the task as whether a given pair interacts at a given time. This is the pair's intensity λuv(t)=λu(t)π(v∣u,t)\lambda_{uv}(t)=\lambda_u(t)\pi(v\mid u,t), how often the source acts times which destination it picks.
  2. Trained. Standard training learns only π\pi, because λu\lambda_u cancels exactly from its optimum.
  3. Tested. The historical and inductive tests compare pairs with different sources, so they need λu\lambda_u.

The three do not agree under either reading of the task. If the task is the pair-level one, training does not learn it. If the task is only which destination a source picks, the stated definitions are wrong, and the historical and inductive tests do not test the task. The pair-level reading is the one that the field's own definitions and tests support, and under it exactly one factor is missing, λu\lambda_u. SNAM supplies λu\lambda_u and nothing else, so all of the improvement comes from this one factor. It is the only term depending on source and time that turns the trained score log⁡π\log\pi into log⁡λuv\log\lambda_{uv}. SNAM is therefore a correction of this disagreement, not a strong feature found on a benchmark.

The experiment you ask for is in Appendix I.6 (Table 26). Each negative is drawn so that its source is as close in activity to the source of its positive as possible. The table gives the gain in test AP from adding SNAM, averaged over five datasets.

Negative samplerActivity gapGain, oursGain, TGNGain, TPNet
DyGLib's historical sampler3.72+6.34+11.65+9.38
Matched on event count1.94+2.02+4.24+3.64
Matched on the rate λu\lambda_u0.24+0.94+0.86+2.10

The activity gap is the average difference in log event rate between the two sources. The gain shrinks as the gap closes. Once the two sources are equally active, this factor is the same on both sides, and nothing is left for it to decide.

AuthorsOpenReview ↗

Q2. A complete architecture diagram

We agree. Because the main contribution of the paper is the diagnosis, an architecture figure does not seem to fit well in the main text. We are preparing one and will add it to the appendix before the end of the rebuttal period.

Reviewer_hZSBOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2(+1)
Soundness
3
Read review
Paper summary

The authors argue that existing temporal link prediction methods concentrate on which node an interaction targets but do not explicitly model whether the source node (i.e., the one the starts the interaction) is active, because standard training settings never reward it. To address this, they propose Source Node Activity Modeling (SNAM), a method that improves predictive performance of temporal link prediction models by estimating how likely a source node is to act at a given time, given its own past history. SNAM estimates a node’s activity from its past interactions across multiple timescales, whose influence fades over time. It is trained with a point-process likelihood that rewards the model for assigning a high score to a node when it really interacts and a low one when it doesn't, across multiple timescales. SNAM can be placed on top of already trained models and improves the performance across different backbones and temporal link prediction datasets, with less than 20 parameters.

Critical strengths
  • The idea behind the method is simple and effective, as SNAM has few parameters and is also efficient. It is also easily portable to existing methods, since it only requires choosing the number of timescales and context blocks, plus a single coefficient β\beta which can be searched on the validation set without retraining the base model.
  • The paper's discussion on current temporal link prediction methods is important, since it explains why the source node's activity has to be learned, yet it is ignored during training. The method is well validated experimentally and shows state-of-the-art or competitive performance.
Critical weaknesses

The overall presentation of the paper could be improved. (i) The core contributions of the paper (i.e., SNAM and the diagnosis) are side in the methodological section, which is mostly dedicated to the deep mathematical description of a backbone architecture the authors introduced (MTHR and CRM). (ii) The notation is hard to follow and shows many terms which seem reused with different meanings.

I strongly recommend improving the presentation of the paper and including a visual illustration of the proposed method, which would help understanding better the contribution.

Questions for authors

In addition, for each question below, please refer to the Weaknesses:

  • Can you discuss the applicability of this method to temporal link prediction on Discrete-Time Dynamic Graphs?
  • Can you please better clarify why you reproduced some baselines and why the results you got are so different from the performances shown in their respective official papers?
  • It is not clear to me whether the three negative sampling strategies of Table 1 are used only at evaluation time, or if they also differ during the training of backbones. If the backbones are trained with the same strategy, could you vary the negative sampling used to train the backbone, to clarify whether the improvement is due to the sampling strategy or to SNAM?
12 comments

Thank you very much for the detailed comments! Your criticism of the presentation was justified, and we took it seriously.

In response, we rewrote the main text from beginning to end, and we rewrote Appendix A.1, which now sets out the core argument step by step. The diagnosis now opens the method section, and the engineering details of our backbone moved to the appendix. The method and the conclusions have not changed.

Before the answers below, please read our two overall responses first, "Clarifying a Likely Misreading of Our Contribution" and "What Changed in the Revised Paper". We believe they are important. They explain what the paper claims and how the revised version is organized, and we hope they already answer many of your questions. We would also be grateful if you could look at the revised paper itself, especially Section 4.1 and Appendix A.1!

AuthorsOpenReview ↗

Q1. The core contributions are overshadowed by the description of the backbone

You are right, and we have reorganized the method section so that the core contributions come first.

Section 4.1 is now the diagnosis. It shows that three things do not agree: the task stated by the benchmark papers (whether a given pair interacts at a given time), the score that standard training produces (which destination a source picks, given that it acts), and what the evaluation protocols test. It also shows that the missing piece is the source's event rate.

Section 4.2 describes the backbone in about one page. Its construction (MTHR and CRM) is now in Appendices C to F.

Sections 4.3 and 4.4 present SNAM, which estimates the missing event rate, and explain how it is added to a trained model.

The abstract, the introduction, and the list of contributions now also start from the diagnosis, and a new first appendix (Appendix A) gives the full argument with proofs. Our second overall response lists these changes.

AuthorsOpenReview ↗

Q2. Notation is hard to follow and symbols seem to be reused

You are right. Most of the notation that was hard to follow came from the engineering details of the backbone, which filled the method section of the submitted version. These details are now in the appendix, so the main text needs far fewer symbols. We also went through the whole revised paper with readability in mind. If any symbol is still unclear, please tell us and we will fix it.

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

This paper identifies a mismatch between random-destination training and temporal link prediction involving comparisons across sources. It derives how preserving the positive example's source and timestamp cancels their shared distribution from the optimal binary discriminator. To recover source activity separately, it introduces Source Node Activity Modeling (SNAM), a multi-timescale Hawkes-type intensity with only K + 1 shared parameters and a closed-form likelihood integral. Its log intensity is added to a relation score with a validation-selected coefficient. The full model combines this component with reusable historical representations and candidate relation modeling. Experiments cover 13 datasets and three negative-sampling protocols, including transfer to four frozen backbones on five datasets.

Critical strengths
  1. The paper provides a useful explanation of what standard negative sampling supervises. The density-ratio derivation connects a concrete training choice to the absence of an absolute source-rate term in the optimal score. This helps explain why improving relation encoders alone need not address cross-source discrimination. Appendix A.1 also correctly distinguishes this conclusion from claiming that learned representations cannot contain activity information.

  2. The transferable correction has convincing practical value. Applying the same fitted activity parameters to four independently trained, frozen backbones isolates a benefit that does not depend on the proposed relation architecture. All 20 historical-negative comparisons in Table 2 improve, and the additional protocols show substantial gains as well. The broader evaluation, component ablations, and shared-hardware timing results provide substantial supporting evidence. The reported checks that zero correction reproduces backbone-only results also strengthen the transfer comparison.

Critical weaknesses
  1. The empirical conclusions remain closely tied to the evaluated negative-source distributions. Historical and inductive sampling change both the relationships being tested and the source distribution of negative examples. Appendix A.1 explicitly retains the negative-pair distribution in the optimal discriminator, while Appendix E.3 explains that AP and AUC are averaged over batches. The reported gains therefore establish usefulness for these sampled cross-source comparisons, but do not yet establish robustness to alternative candidate-source distributions or batch compositions. Controls with activity-matched negative sources and prospective evaluation over fixed time windows would better support the broader interpretation of improved interaction forecasting.

  2. The specific benefit of likelihood-trained SNAM over simpler ways of supplying activity supervision is not fully established. The paper already includes meaningful alternatives: the count-based MLP slightly exceeds SNAM on all five transductive historical-negative datasets in Table 8, and recency is competitive in several settings. SNAM's small parameter count and analytic integral are attractive, but the alternatives are not compared across the frozen backbones, and no held-out assessment establishes the quality of its absolute event-rate estimates. A backbone trained with source-varying negatives would also be an informative control, since the diagnosis directly implicates the training sampler. These comparisons would clarify the contribution of the particular point-process objective beyond the broader value of adding activity information.

Questions for authors
  1. How stable are the gains when varying evaluation batch size and the negative-source distribution? In particular, what happens when negative sources are matched to positive sources by recent activity while retaining different source identities?

  2. On the frozen backbones, how does SNAM compare with the recency and count-based MLP corrections already evaluated on the proposed model, using the same validation procedure? Does held-out event-rate evaluation support interpreting SNAM as an accurate intensity estimator?

  3. If an existing backbone is trained with negatives that also vary the source, or with a mixture of destination-only and source-varying negatives under a matched training budget, how much additional improvement does SNAM provide?

8 comments
AuthorsOpenReview ↗

Opening (please read our two overall responses first)

Thank you very much for this careful and constructive review! We ran every experiment you asked for.

Please read Overall Response 1 first. All our answers rely on it. In short, SNAM is not a technique for raising AP under particular evaluation protocols. It is the correction that makes the trained score agree with the task the field states. The version of the paper you reviewed made it look like such a technique, which was the fault of our writing.

A model trained in the standard way scores which destination a source picks. The task the field states is whether a given pair interacts at a given time. Adding SNAM turns the score of any such model into a score for the stated task, without retraining it. In symbols, the trained score is log⁡π(v∣u,t)\log\pi(v\mid u,t), SNAM adds log⁡λu(t)\log\lambda_u(t) (how often the source acts), and the sum is log⁡λuv(t)\log\lambda_{uv}(t), the rate at which the pair interacts. The gains under DyGLib's historical and inductive negatives are a consequence of this correction, not its target.

AuthorsOpenReview ↗

Q1. Sensitivity of the gains to the evaluation batch size

Averaging AP over batches of 200 positives is DyGLib's standard evaluation, and we keep it so that our numbers can be compared with published ones.

We repeated the evaluation with batches of 50, 100, 500, 1000, and 2000 positives. SNAM improves AP at every size, and under historical negatives the gain does not depend on the batch size. The full results for every dataset are in Appendix I.6 and Figure 8 of the revised paper.

The table gives the gain in test AP from adding SNAM, in points, averaged over five datasets (transductive setting). The columns are the number of positives per batch, and 200 is DyGLib's setting.

NegativesModel5010020050010002000
HistoricalOurs6.246.336.346.266.246.11
HistoricalTGN10.8711.3611.6512.2512.4212.71
HistoricalTPNet9.039.199.389.279.289.13
InductiveOurs6.076.226.205.925.825.48
InductiveTGN10.6611.0411.0210.6510.059.40
InductiveTPNet9.119.449.378.637.976.86
  • Under historical negatives, the gain of our model changes by at most 0.6 points on any single dataset, and that of TPNet by at most 1.3 points. The gain of TGN grows with the batch size because TGN updates its memory once per batch, so its own AP falls as the batches get larger (on UCI from 81.9 to 77.4), while its AP with SNAM stays near 93.
  • Under inductive negatives, the gain is smaller at the largest sizes. This comes from DyGLib's sampler, which fills the batch with randomly drawn node pairs when it runs out of inductive candidates. On Enron these make up 20% of the negatives at 200 positives and 89% at 2000.

The batch size changes how many pairs are compared at once, not which kinds of pairs are compared. A correction of the score should therefore help at every batch size, which is what the table shows.

AuthorsOpenReview ↗

Q2. Dependence on the negative-source distribution; activity-matched negative sources

This control is a direct test of our diagnosis, and we ran it. When the source of each negative is matched in activity to the source of its positive, the gain from SNAM shrinks, and this follows from the task as the field states it. The full results are in Appendix I.6 and Table 26 of the revised paper.

Each negative is drawn from DyGLib's historical pool, with one added condition: its source is a different node that is as close in activity to the positive's source as the pool allows. We measure activity in two ways, by the number of events in the preceding day and by the rate λu\lambda_u itself.

Negative samplerActivity gapGain, oursGain, TGNGain, TPNet
DyGLib's historical sampler3.72+6.34+11.65+9.38
Matched on event count1.94+2.02+4.24+3.64
Matched on the rate λu\lambda_u0.24+0.94+0.86+2.10

The gain is the change in test AP from adding SNAM, averaged over five datasets (transductive setting). The activity gap is the average difference in log event rate between the source of a positive and the source of its negative. At 3.72 the two rates differ by a factor of about 40, and at 0.24 by a factor of 1.3.

The task the field states, whether a given pair interacts at a given time, has only two factors: how often the source acts, and which destination it picks when it acts. Standard training learns the second, and SNAM supplies the first. When the two sources of every comparison are equally active, the first factor is the same on both sides. The test then asks only about the second factor, and even the exact rate of the source would add nothing.

The same control can be applied to the other factor. Suppose each negative were a pair whose destination is as likely a choice for its source as the positive's destination is for the positive's source. The only difference left between positives and negatives would be how active their sources are, and no backbone, however strong, would add much. It would not be reasonable to conclude from this that backbones do not help to predict interactions.

A test of interaction forecasting has to keep both factors. DyGLib's historical and inductive negatives do, and so does the prospective evaluation you suggested, which samples no negatives at all (our answer to Q3). SNAM improves all three models on all five datasets in each of these tests.

Comments on the paper

3 comments
AuthorsOpenReview ↗

Overall Response 1 (Please Read First): Clarifying a Misreading of Our Contribution

We sincerely thank all reviewers for their careful reading! Before the individual answers, we would like to correct an impression that our own submission created.

In the submitted version, the engineering details of our backbone took up most of the method section, and the part we consider most important, the diagnosis, was mostly in the appendix. It is therefore easy to read SNAM as a source-activity feature that raises AP under DyGLib's hard negatives and comes with a mathematical explanation. SNAM is the correction that follows from a contradiction in how the field defines, trains, and tests temporal link prediction, and nothing in it was designed for a particular protocol. The revised paper is organized around this argument (Section 4.1, Appendix A), and we summarize it here.

What is stated. The papers that define the standard benchmarks state the same task. Poursafaei et al. (2022): "to predict the existence of an edge between a node pair at a given time." DyGLib: "predicts the probability of a link occurring between two given nodes at a specific time." TGB: "to predict the property (oftentimes the existence) of a link between a node pair at a future timestamp." In continuous time this is the pairwise event intensity λuv(t)\lambda_{uv}(t), which always factorizes as λu(t)π(v∣u,t)\lambda_u(t)\pi(v\mid u,t), how often the source acts times whom it picks when it acts.

What is trained. Standard training keeps the source and timestamp of each positive and replaces only the destination. The optimum of binary cross-entropy is the log ratio between the distributions of positives and negatives, and both contain λu\lambda_u, so it cancels exactly. Every architecture trained this way learns log⁡π(v∣u,t)\log\pi(v\mid u,t) plus a known term, and more data or capacity cannot change that.

What is tested. DyGLib's random protocol keeps the source of each positive, so it tests π\pi and agrees with training. Its historical and inductive protocols draw complete pairs with other sources, so they require λu\lambda_u, which the trained score does not contain.

One could object that the field never meant the stated task. Suppose it always meant the other task, which destination an active source picks. Then training and the random protocol agree, but all the stated definitions are wrong, and the historical and inductive protocols are not tests of the task at all, because their negatives come from other sources. Their authors introduced them "to evaluate whether a given method is able to predict in which timestamps an edge would reoccur," a question about when a pair interacts, and they read the drop under them as memorization. If the task were destination choice, a model that solved it perfectly would still drop. Whichever task is meant, what is stated, what is trained, and what is tested do not agree.

This is not a matter of wording, because the contradiction costs accuracy that can be measured. TPNet, for example, falls from 96.7 AP under random negatives to 83.9 under historical ones on the five datasets of our transfer study, and adding the one missing factor to the frozen model brings it back to 93.2. AP rises on all 20 backbone-dataset pairs we tested, by up to 25 points.

TGB gives every negative the source and timestamp of its positive, like DyGLib's random protocol, so it also tests π\pi. Yet it defines the task for node pairs, as quoted above, and it applies this protocol to questions such as "whether a flight will happen between two specific airport[s] on a future date," which a ranking of the destinations of one airport cannot answer. The same contradiction is therefore present in TGB, and its protocol cannot show it. No source term can change a TGB result, not even the exact λu\lambda_u, which is why SNAM has no effect there (Appendix A.6).

Only λu\lambda_u is missing, and it is the same for every backbone. SNAM makes what is trained agree with what is stated, for any backbone, with fewer than 20 parameters and without retraining. Adding log⁡λu\log\lambda_u to a score trained in the standard way gives log⁡λuv\log\lambda_{uv} up to a known constant, and λu\lambda_u is also what the historical and inductive tests require. SNAM estimates it from event times by point-process likelihood with K+1K+1 parameters. No negative sample, metric, or protocol appears in its objective. Its output is an event rate, which we now check on held-out events without any ranking metric (Appendix I.5). The performance gains under DyGLib's two protocols are a consequence of the correction, not its target.

We also ran the experiments the reviewers asked for (evaluation batch size, activity-matched negative sources, held-out evaluation of the intensity, backbones trained with historical negatives). They are in the revised appendix and the individual responses, and each result is what the diagnosis predicts.

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Overall Response 2: What Changed in the Revised Paper

The submitted version made SNAM easy to read as a way to raise AP under DyGLib's historical and inductive negatives, so we reorganized the paper. The method and the conclusions have not changed. The diagnosis (Section 4.1) now opens the method section, and the engineering details of our backbone moved to the appendix.

A pair (u,v)(u,v) interacts at time tt at the rate λuv(t)=λu(t)π(v∣u,t)\lambda_{uv}(t)=\lambda_u(t)\pi(v\mid u,t), how often the source uu acts times which destination it picks when it acts. The benchmark papers state the task as whether a given pair interacts at a given time, which is λuv\lambda_{uv}. Standard training learns only π\pi. SNAM supplies the missing λu\lambda_u from event times, and no negative sample, metric, or evaluation protocol appears in its objective.

Reorganization

  1. Sections 4.1 and 4.2; backbone details in Appendices C to F. Standard training replaces only the destination of each positive, so λu\lambda_u cancels exactly from the optimal score. Every model trained this way scores which destination a source picks and says nothing about how often the source acts.
  2. Table 7. If the task is "does this pair interact at this time", standard training does not learn it. If the task is "which destination does an active source pick", the benchmark papers' definitions are wrong, and DyGLib's historical and inductive tests do not test it, because their negatives come from other sources. Either way, the definition, the training, and the tests do not agree.
  3. The drop from random to historical or inductive negatives is not a failure to generalize. A perfectly trained model with unlimited data has the same drop (Proposition 2).
  4. Table 9. Adding log⁡λu\log\lambda_u is forced by the task definition. It is the only term depending on source and time that turns the optimal training score, log⁡π\log\pi, into log⁡λuv\log\lambda_{uv} (Proposition 4). With its weight fixed to the theoretical value 1 and nothing tuned, AP under historical and inductive negatives rises on all 13 datasets (transductive setting).
  5. Table 10. Count-MLP's slightly higher AP under DyGLib is an artifact of how DyGLib tests, and Count-MLP cannot recover the pair's rate λuv\lambda_{uv} that the task defines. Count-MLP is itself a classifier trained against sampled negatives and estimates the fraction of all events at time tt that come from source uu, λu(t)/Λ(t)\lambda_u(t)/\Lambda(t), not the rate λu(t)\lambda_u(t). DyGLib scores models only at timestamps where an interaction occurred, so its tests are built on exactly this fraction.
  6. TGB states the task for node pairs and trains with the same destination replacement, so its models also lack λu\lambda_u, and its test cannot show this. Every TGB negative shares the source and timestamp of its positive, so no source term can change a TGB result, not even the exact λu\lambda_u.
  7. The new Appendix A, "Why This Is Not Metric Hacking on DyGLib", sets out points 2 to 6 in full.

New experiments requested by the reviewers

  1. Backbones retrained with half of the negatives historical (Section 5.3, Table 3, Appendix A.3). Training with historical negatives fits the score to the historical-negative test at the expense of the random-negative test, and brings it no closer to λuv\lambda_{uv}. It raises AP under historical and inductive negatives and lowers it under random negatives on every dataset. Adding SNAM to the standard-trained model lowers nothing.
  2. Held-out check of the intensity (Appendix I.5). SNAM's output is an event rate, and it is accurate as one. The check uses held-out event times only, with no negative sample, ranking metric, or backbone. Between two consecutive events of a source, SNAM predicts 0.92 to 1.02 events on average, where a correct rate predicts 1.
  3. Evaluation batch size and activity-matched negatives (Appendix I.6). The gain from SNAM tracks how different in activity the two compared sources are. It does not depend on the batch size under historical negatives. When each negative's source is as active as its positive's, the gain of our model shrinks from 6.3 to 0.9 points. The task defines λuv\lambda_{uv}, which has only two factors, λu\lambda_u and π\pi. This test makes λu\lambda_u nearly equal within every comparison and so removes one of the two, and the gain from supplying it naturally shrinks. Negatives matched on destination choice would likewise leave a backbone with little to contribute.
  4. Prospective evaluation over fixed time windows (Appendix I.7). The gain also appears when no negatives are sampled at all. Each model scores all previously observed pairs at the start of a time window, and the pairs that interact in the window are the positives. SNAM raises AP for our model, TGN, and TPNet on all five datasets, in all 45 runs (TPNet on Wikipedia, 2.9 to 20.0).

An architecture figure is in preparation.

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Architecture figure added (Figure 9, Appendix J)

As Reviewers hZSB, BLnH, and LCkt suggested, we have added an architecture figure: Figure 9 in Appendix J, on the last page of the revised PDF. Panel (a) shows the diagnosis and panel (b) the model.

The rest of the paper is unchanged except for one reference to this figure in Section 4, so all section, table, and figure numbers cited in our earlier responses remain valid.

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

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