acceptodds
Under review as a conference paper at ICLR 2027

Do Temporal Link Predictors Need Learned Memory? A Smoothed-Count Baseline with a Handful of Parameters

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Abstract

Many temporal link predictors summarize past interactions through learned node representations. We examine whether simple counts of recurring interaction patterns can provide competitive predictions without learning these representations. We propose a temporal link predictor based on statistical language modelling. It pools transition and co-occurrence counts across sources to predict links that a source has never formed. We smooth sparse estimates using destination frequencies or Kneser-Ney continuation counts. A shared log-linear rule combines these estimates with popularity, source history, and recency, without node embeddings. In our main evaluation, the model achieves the highest MRR among the compared methods on 7 out of 16 datasets from TGB and TGB-Seq. It also outperforms EdgeBank and Base3 on all 16 datasets and the heuristic family on 14. These gains extend to datasets designed to limit repeated edges. With only 9–13 learned parameters, our model provides a simple and competitive baseline for evaluating future neural temporal link predictors.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
temporal link prediction, temporal graphs, statistical language modelling, backoff smoothing, log-linear models

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_bKogOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper considers the temporal link prediction (TLP) and proposes a lightweight log‑linear temporal link predictor without node embeddings. Inspired by language‑model smoothing, it uses pooled transition and co‑occurrence counts. Even with 9‑13 learnable parameters, it can achive inference quality competitive to or even better than existing TLP approaches on TGB and TGB‑Seq benchmarks.

Critical strengths

S1. The basic idea of examining whether simple counts of recurring interaction patterns can provide competitive predictions without learning these representations seems interesting.

S2. This paper anonymously provides its code and data to ensure reproducibility of experiments.

Critical weaknesses

W1. It seems that this paper does not provide a comprehensive formal statement regarding the considered TLP problem.

First, it is unclear this paper considers which data model of dynamic graphs, e.g., discrete-time dynamic graphs (DTDGs) and continuous-time dynamic graphs (CTDGs), as different data models may have different experiment settings and evaluation protocols.

Second, it is unclear whether this paper assume graph attributes (e.g., node attributes) are available. It seems that the simple method proposed by this work does not consider attributes, while some baselines in experiments (e.g., DyRep, TGN, DyGFormer, etc.) can leverage such attributes.

Third, it is unclear this paper considers the conventional transductive or advanced inductive settings of TLP or both. It seems that the proposed method can only support the transductive TLP, while some baselines in experiments (e.g., DyRep, TGN, CAWN, DyGFormer, etc.) can handle inductive TLP, predicting future links for new nodes not observed in previous time steps.


W2. The overall presentation of this paper is still hard to understand (e.g., lack of details about toy example figures and necessary preliminaries), which need significant improvements.

It should be a good presentation to show the basic motivation using Fig. 1 at the very beginning. However, it seems that Fig. 1 is LLM-generated cluttered with many mathematical notations. There seem no further descriptions regrading Fig. 1's details, e.g., what do different notations like zz, uu, P^\hat P, etc. mean, how to get such a toy example from which dynamic graph, etc. As a result, it is still unclear what do Fig. 1 mean even after reading Section 1 (Introduction).

It was claimed that this work utilizes some classic techniques in NLP (e.g., statistical language modelling, Kneser-Ney continuation counts, etc.) to tackle TLP. However, there seem no preliminaries about these techniques, e.g., toy examples about the mapping from text corpus to dynamic graphs, formal definitions of each concept. In particular, it remain unclear how these NLP techniques are applied to dynamic graphs and why they can help ensure the quality of TLP. Such a presentation issue makes the basic motivation of this paper very weak and hinders a comprehensive evaluation regarding the novelty.


W3. Consistent with W2, there seem no pseudo-code to describe the overall training and inference procedures of the proposed method. As a result, it is still hard to understand how this method exactly work.


W4. There seem no any formal analysis of complexity or empirical runtime evaluations for the proposed method.

It was highlighted that the proposed method only has 9-13 learned parameters, indicating that it is a lightweight yet effective method. While it cannot ensure the best inference quality in all cases, it is expected to achieve much better inference efficiency or scalability compared with most baselines, especially those with much more learnable parameters. In this sense, a significant trade-off between the inference quality and efficiency/scalability should be a potential advantage of the proposed method. Nevertheless, there seem no complexity analysis or runtime evaluations to validate this advantage.


W5. Some details about experiments are missing.

There seems no summary about the statistics of datasets using in datasets, e.g., numbers of nodes, edges, time steps, etc..

There seem no descriptions regarding the experiment environment, e.g., OS, CPU, GPU, memory size, etc.

Questions for authors

See W1-W5.

3 comments
AuthorsOpenReview ↗

Response to Reviewer bKog

Thank you for recognising the interest of testing recurring interaction counts and the reproducible code release. We have expanded the explanations and added pseudocode, cost measurements, and dataset statistics. The added text is blue.

W1

We have expanded Sec. 3 (blue). Our model takes continuous-time events (u,v,t)(u,v,t), using node IDs and timestamps without attributes.

The heuristics and CRAFT also use no attributes. CRAFT leads on the most datasets among our neural references (Yi et al., 2025a). TGN can use node and edge attributes (Rossi et al., 2020), while TPNet uses edge features in its released implementation (Lu et al., 2024).

Our model supports both transductive and inductive prediction with a fixed candidate vocabulary. Its shared weights can score nodes seen during training and nodes first observed afterwards. TGB also includes new nodes during validation and testing (Huang et al., 2023, App. G). We report overall test MRR rather than separate scores for seen and unseen nodes.

W2

We have redrawn Fig. 1 with node lanes and time columns. Arrows connect sources u,u′u,u' to targets. Source uu visits a,b,c,b,ca,b,c,b,c, and u′u' visits dd. The caption defines the candidate zz and smoothed estimate P^\hat{P}. App. E now substitutes the counts: with no decay and α=1\alpha=1, P^tr(c∣b)=(2+0.30)/(2+1)≈0.77\hat{P}_{\mathrm{tr}}(c\mid b)=(2+0.30)/(2+1)\approx0.77. There are two b→cb\to c transitions, and 0.30 is the smoothed frequency of cc.

Sec. 4.1 explains the estimators through film examples. Targets act as words and each source sequence as a sentence. Single targets are unigrams and consecutive pairs are bigrams. These pairs describe successive interactions of one source, not graph edges between targets. Pooling across sources lets one viewer's transitions support a film another has never watched. Co-occurrence also includes pairs separated by other visits.

Sec. 4.2 also explains smoothing. Popularity remains a separate feature, while smoothing keeps each estimate positive for its logarithm and gives backoff more weight when counts are sparse. Marginal backoff uses target frequency. Continuation backoff counts distinct predecessors: b,cb,c occur equally often, but bb has two predecessors and cc one. If no transitions from a recent target have been observed, its transition estimate equals the backoff.

W3

We have added pseudocode for feature extraction, training and inference in App. G.1 (blue), referenced in Sec. 4.5.

We process training and validation events in order. For each event, we compute candidate features from the preceding interactions, save them, then update the counts and recent history. These features are computed once. Training adjusts only the shared scoring parameters, using the saved training features and one uniform negative per query. Validation MRR selects the best parameters. Training stops after ten epochs without improvement or at 100 epochs.

At test time, we initialise history from the training and validation events. The fitted parameters remain fixed. We score each query from preceding interactions, then add its observed event to history.

W4

We have added runtime, memory and complexity results in App. J (blue). On tgbl-enron, where all methods completed three uninterrupted fits, mean preparation and fitting take 42.5 seconds for ours, 649.6 for CRAFT and 781.5 for TGN. All use an L40, with EPYC 7763 for ours/TGN and 7543 for CRAFT. We compute features once and reuse them across epochs, fitting only the shared scoring parameters.

Prediction requires computing features for each new query. Ours predicts faster than TGN on GoogleLocal and YouTube, while TGN is faster on tgbl-enron. CRAFT is faster on all three. Our peak allocated GPU memory is lower than both, while process RAM is higher on GoogleLocal and YouTube (Tab. 9). App. J reports three runs for counting methods on all 16 datasets and neural prediction on these three, separated by CPU type.

For MM candidates and KK recent interactions, feature construction and scoring take O(M(K+1))O(M(K+1)) time under expected constant-time hash access. Basic count updates take O(1)O(1) per event, and co-occurrence adds O(K)O(K). At fixed KK, count storage can grow linearly with the number of events. Training also stores candidate features for reuse across epochs. App. J.1 derives the full storage and fitting costs.

W5

We have added Tab. 3 in App. A (blue), reporting source and target nodes, interaction events, distinct directed pairs and distinct timestamps for all 16 datasets.

App. G specifies one L40 GPU, four allocated CPUs and 128 GiB of allocated RAM per main fit. The cluster runs Debian GNU/Linux 13. App. J gives the runtime setup: four CPU threads on EPYC 7543/7763, L40 GPUs for comparisons with neural methods, Python 3.13.5, PyTorch 2.11.0+cu128, NumPy 2.5.1 and CUDA 12.8.

Thanks for the rebuttal, which address some of my concerns. However, W2 about the overall presentation may still not be well addressed. I decide to keep my original score.

Thank you for confirming that the rebuttal addresses some of your concerns. We would like to understand which part of W2 remains unclear in the revised manuscript. Your original comment identified two specific presentation issues, and we revised both:

  • Fig. 1 now shows a bipartite user–film graph with nodes in lanes and time in columns. Arrows connect users to films, rather than suggesting graph edges between successive targets. The caption defines the sources, candidate, recent targets, probability estimates, recency and scoring parameters. App. E shows how the example counts enter the equations, including the calculation of the transition probability of approximately 0.77.
  • Sec. 4.1 now explains the connection to language modelling through film examples. Each source supplies a sequence of targets, corresponding to a sentence of words. Individual targets give unigram counts and consecutive pairs give bigram counts. Pooling these across sources allows another viewer's transition to support a film the current viewer has never watched. We also explain how co-occurrence includes nonconsecutive pairs. Sec. 4.2 introduces smoothing and explains both backoff distributions through the same examples.

These changes are marked in blue in the revised manuscript. Could you point to the specific passage, notation, or step that remains unclear? This would allow us to address the remaining presentation concern directly within the time available for discussion.

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

This paper is about designing a baseline that uses a set of statistical summary features for temporal link prediction. The authors argue that this simple and intuitive approach which is carefully constructed from 1) pooling destination-transition and 2) windowed co-occurrence counts, combined with destination popularity, source-specific interaction counts, and recency-based features, are in fact superior to learned node representation-based methods for certain datasets from TGB. They also compare against other simpler feature-based baselines like edgebank and base3, and show their approach is superior in terms of predicting links on MRR metric. The paper also presents a number of ablations and sensitivity analysis to their approach.

Critical strengths
  1. A simple, intuitive approach based on featurizing prior node interaction in a temporal graph. The observations made by the authors for motivating the features are clear and sound. The proposed method has very few learned parameters and compared to featurization based baselines like EdgeBank and Bae3, a large majority of the datasets chosen from TGB benchmark show good improvement in terms of MRR using their method.

  2. The feature decomposition approach taken by the authors in the paper can serve as a good diagnostic tool to provide insights in the dataset for practitioners in the domains of temporal link prediction. The feature ablations, coefficient signs, coverage measurements adapted from this proposed method could help obtain a deeper understanding of not only TGB but other domain specific datasets for which link prediction is being performed. and moreover, the featurization proposed is inexpensive.

Critical weaknesses
  1. The proposed methods advantage over learned node representations is very dataset dependent and not universal as shown in the experiments. So IMO it limits the broad interpretation that memory and learned representations are not useful. From Table 1 and Table 2, the majority of the winners are still neural based methods. In fact, for many of the datasets like tgb-comment, tgb-review, the best neural benchmarks win by a wide margin compared to the proposed approach, so motivated featurization does not completely cover the many other underlying statistics. So, I still view this proposed approach as an improved statistical baseline / diagnostic method.

  2. A potential extension is to incorporate the proposed approach into the architecture of the neural predictor end to end and maybe it would reveal the complementary information the proposed approach captures which neural models miss.

Questions for authors
  1. Can the authors confirm if the same history windows for the neural baselines were used compared to the proposed approach during experimentation ? Could not find it in the main text.
2 comments
AuthorsOpenReview ↗

Response to Reviewer frhv

Thank you for recognising the motivation for the features, the small parameter count, and the gains over counting baselines. We also appreciate your assessment of the ablations, coefficient signs, and coverage measurements as useful diagnostics. We have revised the contribution statement, clarified history access, and added your proposed extension as future work. These changes are blue.

W1

Your description of the model as an improved statistical baseline and diagnostic method captures our intended contribution. A useful baseline need not outperform every neural method on every dataset. It helps establish where simple statistics suffice and where learned history representations offer further gains.

With only 9–13 learned parameters, our model achieves the highest MRR on seven of sixteen datasets in Tab. 1 and 2. This is the largest first-place count in our comparison, followed by CRAFT and CRAFT-R with six combined. Against the counting baselines, it exceeds EdgeBank and Base3 on all 16 datasets and the heuristic family on 14 under both event-wise and batch-200 updates. These results support its value as a reference beyond repeated-edge prediction, since pooled transitions can support links a source has never formed.

The advantages of neural methods on tgbl-comment and tgbl-review are consistent with this role. Our results do not establish that learned memory is generally unnecessary. We have revised Sec. 7 in blue to state that performance depends on the dataset and to present the model as a simple and competitive baseline against which future neural temporal link predictors should be evaluated.

W2

Your suggestion is useful because our standalone comparisons do not test whether the statistics and learned representations work better together. We have added this direction as future work in Sec. 7 (blue).

One option would feed our statistical features into TGN's prediction network alongside the source and target embeddings (Rossi et al., 2020, Sec. 5). For CRAFT, the features could accompany its cross-attention representation and temporal features at the prediction network (Yi et al., 2025a, Sec. 4.1). The neural components could be trained jointly while the count-update rules remain fixed.

Comparing each predictor with and without these features, using the same data, candidates, history access and training budget, would test whether the statistical estimates improve its predictions.

Q1

Our experiments use the chronological training, validation and test splits supplied by TGB and TGB-Seq, together with their negative candidates and MRR evaluation. The neural references are reported benchmark results from the original studies and leaderboards. App. A documents their sources and evaluation details. Sec. 3 and the revised Tab. 1 caption now make this basis of comparison easier to locate.

Comparing against reported benchmark results follows established practice. CRAFT uses previously reported TGB and TGB-Seq baseline scores (Yi et al., 2025a, Sec. 5.1). CTAN takes its Tab. 11 TGB baseline scores from an earlier study (Gravina et al., 2024, ICML). KEAT takes its Tab. 1 baseline scores from the TGB leaderboard (Waghmare et al., 2026, AAAI).

App. I additionally compares our model and the recomputed counting baselines under the same event-wise and batch-200 update schedules. Our gains over the counting baselines persist under both schedules.

Thanks to the authors for providing comments on the questions raised during review period, I wish to keep the score the same as I already sway towards acceptance. Appreciate the additional color / discussion for W2 in the paper.

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

The paper investigates whether competitive temporal link prediction can be achieved without learned node embeddings. It proposes a statistical model based on how often and how recently nodes interact, which destinations follow one another, and which destinations appear close together in past interactions. Sparse conditional estimates are smoothed toward either marginal destination frequencies or a Kneser-Ney-inspired continuation distribution. A shared log-linear scoring rule then combines these estimates and recency features with 9–13 learned parameters. Experiments are done to validate the effectiveness of the proposed method.

Critical strengths
  1. The problem studied is relevant to temporal graph learning. A strong statistical baseline helps determine what learned representations contribute beyond familiar interaction patterns. Extending this question to TGB-Seq, where several datasets restrict repeated edges, is particularly useful. With comprehensive and rigorous evaluations, this may serve as a valuable baseline in temporal link prediction.

  2. The model is explicit and interpretable. The equations specify the count estimators, smoothing distributions, recency features, and scoring rule. The worked example in Figure 1 and Appendix E helps readers understand the method more easily; its displayed estimates and ranking are consistent with the stated equations.

  3. The observation that marginal and continuation backoff behave differently across datasets is informative, as this is usually a critical factor to consider in temporal link prediction.

Critical weaknesses
  1. The proposed method does not seem to outperform state-of-the-art learning methods. From Table 1 and Table 2, we can see that sometimes its performance is not very competitive, especially in TGB-Seq benchmark, where the setting is more critical for link prediction. In addition, some comparisons differ in candidate sampling and available history. Under updates every 200 events, the proposed method's MRR drops from 82.84 to 74.08 on tgbl-wiki and from 39.00 to 31.63 on ML-20M. Its reported dataset wins fall from seven to four.

  2. The results depend heavily on how events with identical timestamps are handled. The main evaluation allows earlier rows at a timestamp to inform predictions for later rows at that same timestamp. Removing this information reduces MRR from 86.83 to 53.50 on tgbl-enron. Different orderings of events seem to have a great impact on the performance, which may not be desirable in practice.

  3. The computational and storage costs are not adequately reported. The small number of learned parameters does not capture the cost of storing interaction counts, transition tables, co-occurrence tables, recent histories, and cached features. The paper is expected to report peak memory use, feature-extraction time, fitting time, and prediction speed on a large dataset. It may also explain how these costs grow with the number of interactions and the history-window size.

  4. The experimental results need to be more comprehensive. Complete results for all the baseline methods should be presented under consistent evaluation settings. The component comparisons may also include a simpler model using only destination popularity, source history, and recency, with the same weight-fitting procedure. This would help establish how much transitions and co-occurrences contribute.

  5. More illustrative examples can be provided to make the method easier to understand. The paper introduces several types of counts, smoothing rules, and scoring features. Illustrative examples of these parameters together with how they are used in the equations would be helpful.

Questions for authors

Please kindly refer to the weaknesses.

3 comments
AuthorsOpenReview ↗

Response to Reviewer bWgr

Thank you for recognising the value of an interpretable baseline on TGB-Seq and the backoff analysis. We have added fitted controls, an event-order experiment, and cost measurements. The text additions are blue.

W1

Our contribution is a baseline for measuring what learned history representations add, not a claim that they are unnecessary. A useful baseline need not outperform every neural method on every dataset. Nevertheless, with only 9-13 learned parameters, our model achieves the highest MRR on seven of sixteen datasets in Tab. 1 and 2. This is the largest first-place count, followed by CRAFT and CRAFT-R with six combined. Sec. 7 states this scope.

TGB and TGB-Seq define benchmark splits, negative sampling and MRR. App. A documents the reported neural scores and settings. CRAFT also takes baseline scores from previous studies (Yi et al., 2025a, Sec. 5.1). With batch-200 updates, our model retains four first-place results against the reported references, second only to CRAFT and CRAFT-R.

Rossi et al. (2020, Sec. 3.2) describe TGN batches of 200 as "a good trade-off between speed and update granularity". Feldman and Baskin (2025, Secs. 5.1-5.2) separate prediction batches from updates and use a "memory batch size of 1" in LDTGN. Our model likewise computes features from past interactions, then adds the current event to history. Saved features can be scored in batches. Using observed test events for later predictions follows TGB's streaming setting (Huang et al., 2023, App. C). Sec. 5 and App. I now explain this distinction. With weights and candidates fixed, the reductions you cite measure the effect of delayed updates.

W2

Our gains over EdgeBank and Base3 persist on all 16 datasets under both event-wise and batch-200 updates, and over the heuristic family on 14. Candidates and update schedules are identical for each method within each comparison (App. I, Tab. 6 and 7). The strict-timestamp results show that access to observations at the prediction timestamp matters particularly on tgbl-enron, WikiLink, Flickr and YouTube.

To investigate this sensitivity further, we evaluated 100 random orders within tied test timestamps on each dataset. We keep weights from five training seeds, candidates, and training/validation order fixed. On 12 datasets, every sampled order changes MRR averaged across seeds by less than 0.17 points. The four remaining datasets also have the largest strict-timestamp reductions. Sec. 5 now states the update and file-order conventions, and App. L, Tab. 10 reports the new results.

W3

Training is faster on tgbl-enron: mean preparation and fitting take 42.5 seconds for ours, 649.6 for CRAFT and 781.5 for TGN. All three methods completed three uninterrupted runs there. Other neural runs required resumption after job interruptions. Our features are computed once and reused across epochs. All use an L40, with EPYC 7763 for ours/TGN and 7543 for CRAFT.

We also report large-dataset costs on tgbl-comment (44.3 million events). Feature extraction takes 50.4 minutes, fitting with validation 42.0 minutes, and batch-200 CPU test prediction 19.3 minutes. Peak process RAM during extraction is 27.0 GiB, including data and history. These are means over three runs.

App. J reports prediction time and memory on all 16 datasets. Ours predicts faster than TGN on GoogleLocal and YouTube. TGN is faster on tgbl-enron, and CRAFT is faster on all three. Test timers include all prediction work and transfers, excluding loading and initial history construction.

App. J.1 accounts for counts, histories and cached features. For MM candidates and a context of KK recent interactions, features and scores take O(M(K+1))O(M(K+1)) time. Co-occurrence adds up to K updates per event. At fixed K, count storage can grow linearly with events. Caching stores one feature vector per training and validation candidate.

W4

We discuss the benchmark protocols and baseline settings in our response to W1.

New App. K, Fig. 12 compares:

A: popularity, source history and recency. B: A + transitions. D: A + co-occurrence. C: A + both.

All four use the same fitting procedure, marginal backoff, data and evaluation settings, with three training seeds per dataset.

B, D and C each improve A on 15/16 datasets, including all seven TGB-Seq datasets. Median gains are 3.27, 3.76 and 4.96 MRR points, respectively. The median gain from either feature type is smaller when the other is already included. Pooled transition and co-occurrence counts thus improve an already fitted baseline.

W5

Following your suggestion, Fig. 1 now shows source-to-target edges, with node lanes and time columns. Its caption defines the symbols. Secs. 4.1-4.2 explain the estimators and smoothing through film examples. App. E substitutes the counts into Eq. (1): with no decay and α=1\alpha=1, two b→cb\to c transitions give P^tr(c∣b)=(2+0.30)/(2+1)≈0.77\hat{P}_{\mathrm{tr}}(c\mid b)=(2+0.30)/(2+1)\approx0.77. Marginal backoff assigns 0.30 of the one virtual observation to cc.

Thank you for the responses. I am still not sure why we need a new baseline if the observation is simple but the performance is not convincing enough. Thus, my score remains.

Thank you for the follow-up. Your initial review identified an important role for statistical baselines: determining what learned representations contribute beyond familiar interaction patterns. Our contribution directly addresses that question.

With only 9–13 learned parameters, our model achieves the highest MRR on 7 out of 16 datasets from TGB and TGB-Seq in the main comparison. This is the largest first-place count, followed by CRAFT and CRAFT-R with six combined. It also exceeds EdgeBank and Base3 on all 16 datasets and the heuristic family on 14 (Tabs. 1–2).

Following your suggestion, we ran additional experiments against a fitted model using only popularity, source history and recency. Adding transitions and co-occurrence improves 15 of 16 datasets, including all seven TGB-Seq datasets, with a median gain of 4.96 MRR points over three training seeds (App. K). This establishes a contribution beyond fitting weights to the simpler features.

These findings explain why the new baseline is useful. An improvement over EdgeBank or Base3 alone does not establish that learned node representations are needed to achieve that performance. Our model provides a more competitive statistical reference for assessing those gains. Its simplicity makes the comparison easier to interpret, while the experiments establish the predictive value of the proposed components.

Could you clarify which comparison or result you consider insufficient to support this contribution? This would help us address the remaining concern directly.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Comment to the Area Chair

Dear Area Chair,

Our paper develops a statistical temporal link predictor with 9-13 learned parameters. The reviewers recognised the value of an interpretable baseline and backoff analysis (bWgr), the feature motivation and diagnostic analyses (frhv), and the interest of the approach and its reproducibility (bKog).

Alongside these positive assessments, the reviewers offered constructive suggestions. We responded with substantial new experiments, three new appendices, and a rewritten method explanation. These additions address the following points. Revised text is blue.

  • To make the method easier to understand, we rewrote Section 4.1, expanded the smoothing explanation in Section 4.2, and redrew Figure 1 to show source-to-target interactions. Movie rating examples and calculations in Appendix E connect the statistics to their equations (responses to bWgr W5 and bKog W2).

  • To establish what the two modelling ingredients transitions and co-occurrence contribute, we trained additional control models on all 16 datasets with three training seeds and compared four fitted configurations (new Appendix K). The results support our point that both mechanisms are needed beyond fitting weights to popularity, source history, and recency (response to bWgr W4).

  • To examine the sensitivity of our method to the distribution of timestamps within batches, we ran new evaluations of 100 shuffled orders on every dataset, shuffling only events with equal timestamps (new Appendix L). Results are not affected in 12 out of 16 datasets. We also clarified the benchmark inputs and update schedules in Sections 3 and 5 and Appendix I. Gains over the counting baselines persist under both event-wise and batch-200 updates (responses to bWgr W1, W2, W4 and frhv Q1).

  • To measure costs beyond the parameter count, we ran additional runtime and memory experiments on TGB and TGB-Seq and report them in the new Appendix J. Our results show that fitting our method is more than one order of magnitude faster than training the fastest neural method. Inference times are comparable and even faster in some of the datasets (responses to bWgr W3 and bKog W4).

  • To imporve the reproducibility of our results, we expanded Section 3 and added training and inference pseudocode, dataset statistics, and hardware and software details in Appendices A and G. We also clarified the contribution as a competitive baseline and added the proposed combination with neural predictors as future work in Section 7 (responses to bKog W1, W3, W5 and frhv W1-W2).

We thank the reviewers for these constructive suggestions. We believe the new experiments strengthen the evidence for our model, while the rewritten explanations and added implementation details make it easier to understand, assess, and reproduce.

Dear Area Chair,

We would appreciate your attention to the discussion with reviewers bWgr and bKog. Reviewer bWgr recognised the value of an interpretable statistical baseline and the backoff analysis. Reviewer bKog found the approach interesting and acknowledged its reproducibility. Alongside these positive assessments, both reviewers requested additional evidence and clearer explanations.

In response, we made substantial additions:

  • We ran the requested comparison against a simpler fitted model across all 16 datasets. Adding transitions and co-occurrence improves 15 datasets, including all seven TGB-Seq datasets, with a median gain of 4.96 MRR points (App. K).
  • We added runtime and memory measurements, together with a computational complexity analysis (App. J).
  • We evaluated 100 shuffled event orders on each dataset to investigate timestamp sensitivity (App. L).
  • We rewrote the method explanation, revised Fig. 1, and expanded the worked examples.

Reviewer bWgr's follow-up maintains the score because the reviewer remains unconvinced about the need for the baseline and its performance. However, it does not discuss these additions or explain which evidence remains insufficient. The main comparison shows that our model exceeds EdgeBank and Base3 on all 16 datasets and achieves the highest MRR on seven, the largest first-place count among the compared methods.

Reviewer bKog has acknowledged that the rebuttal addresses some concerns, but maintains the score because W2 on presentation "may still not be well addressed." We rewrote Secs. 4.1–4.2, redrew Fig. 1, defined its notation, and expanded the worked examples in response to W2. The follow-up does not identify which passage or explanation remains unclear. A specific example would allow us to respond directly.

The ICLR 2027 Reviewer Guide states that a lack of state-of-the-art results is not, by itself, grounds for rejection. It asks reviewers to assess the knowledge contributed, engage actively in discussion, remain open to revising recommendations, and explain what did or did not change their assessment. We would appreciate consideration of our contribution and revisions on this basis.

Both follow-up comments arrived only hours before the discussion deadline, leaving little time to clarify the remaining concerns through further discussion. We would therefore appreciate your independent assessment of the revised manuscript and additional evidence, particularly whether they address the original requests and substantiate the value of the proposed baseline.

We thank the reviewers for the suggestions that helped us strengthen the paper, and you for considering these revisions in the final assessment.

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

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