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REVIEW 3 major objections 5 minor 50 references

Revisiting the Necessity of Graph Learning and Common Graph Benchmarks

T0 review · 3 major / 5 minor · reviewed 2026-08-11 · deepseek-v4-flash

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Pith's one-line read A well-tuned feature-only MLP nearly matches graph neural networks on five of seven common graph benchmarks.

desk verdict Useful feature-ablation study and synthetic benchmarks, but the headline claim about graph structure is undercut by uncontrolled comparisons; conditional acceptance. read the letter →

arxiv 2412.06173 v1 pith:PQGXPSKM submitted 2024-12-09 cs.LG stat.ML

Isay Katsman , Ethan Lou , Anna Gilbert This is my paper · ORCID
classification cs.LGstat.ML
keywords graphneuralnetworksnodeclassificationlinkpredictionbenchmarkevaluationfeatureleakageMLPbaselinesyntheticdatasetsstructurenecessity
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

Graph machine learning assumes node features and graph structure are separate, so that benchmark scores show what models learn from the graph. This paper challenges that assumption across seven of the most widely used graph datasets, finding that a carefully tuned feature-only MLP matches or beats many graph neural networks on five of them. The paper argues those five datasets are weak instruments for measuring graph-learning progress because their node features already contain enough graph information to make the graph nearly redundant. If the finding holds, much of the published benchmark comparison on these datasets should be re-interpreted with a properly tuned MLP baseline in hand.

What carries the argument

The load-bearing instrument is the feature-ablation comparison: for each dataset, the authors create variants with increasing numbers of node features, then tune both an MLP and a GCN on each variant and track how the accuracy gap moves. When the gap collapses as features are added, the features are said to leak the graph structure, explaining why the full-feature MLP nearly matches graph methods. The complementary machinery is a parametric family of synthetic Watts-Strogatz datasets, $\mathrm{WS}1000_\gamma$, whose features are generated with a tunable parental dependence along the graph, so the graph's necessity can be controlled from first principles.

What would settle it

On Amazon Computers, re-tune GCN, GAT, and DAGNN with the same split and the same hyperparameter budget used for the tuned MLP; if the re-tuned graph models outperform it by more than the paper's reported gap, the 'little benefit' claim fails.

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Extended reading notes

Core claim

The paper's central claim is that on Amazon Computers, Amazon Photo, Coauthor CS, Coauthor Physics, and PubMed, the graph adds little beyond the node features: a well-tuned MLP that never sees the graph reduces error by up to 70% relative to previously reported MLP baselines, and on Coauthor Physics it outperforms almost every graph-based method tested. The mechanism is not that graphs are useless, but that the features leak graph information: as the paper feeds the MLP and a GCN increasing subsets of the features, the performance gap between them closes for these datasets while staying roughly constant for Cora, where the graph still matters. Based on this, the paper proposes a parametric family of synthetic Watts-Strogatz link-prediction datasets in which informative features are generated by graph-dependent parental dependence, and identifies Cora, CiteSeer, Musae-Twitch, Twitch-PTBR, and Musae-Facebook as real-world tasks with a meaningful MLP-versus-GCN separation.

Load-bearing premise

The analysis assumes that the graph-network accuracies taken from earlier papers were obtained under training and evaluation protocols equivalent to those used for the tuned MLP, so the reported gaps are a fair head-to-head comparison rather than an artifact of different splits or tuning budgets.

Editorial extensions

If this is right

  • Five of the seven most common graph benchmarks—Amazon Computers, Amazon Photo, Coauthor CS, Coauthor Physics, and PubMed—should no longer be treated as demonstrations that graph structure matters, without a strong tuned-MLP baseline.
  • Reported gains of graph networks on these datasets may largely reflect hyperparameter tuning rather than graph-specific architecture, so a tuned MLP should be a required point of comparison in future evaluations.
  • Cora, CiteSeer, and the Musae-Twitch, Twitch-PTBR, and Musae-Facebook link-prediction tasks offer real-world settings where the graph provides a clear, measurable benefit.
  • The synthetic WS1000 family gives the field a controlled testbed where graph information is necessary by construction, allowing researchers to measure how much a method actually exploits structure.
  • Benchmark designers should screen new datasets for feature leakage by running the MLP-versus-GCN gap at increasing feature counts before adopting them.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • If the feature-leakage mechanism generalizes, other feature-rich node-classification datasets—especially those with bag-of-words or product-description features—could exhibit the same effect, so a tuned MLP could serve as a cheap screening test before any new graph dataset is adopted.
  • The synthetic generation procedure could be extended beyond link prediction to node and graph classification, letting researchers dial the parental-dependence parameter to calibrate how much structure a method truly requires.
  • A practical red-flag tool falls out of the feature-ablation comparison: a gap that shrinks as feature counts grow is a warning that reported GNN advantages on the full dataset may not be driven by graph structure.
  • Re-tuning the graph baselines on identical splits with the same budget as the MLP would either confirm the paper's conclusion or reveal that part of the 'little benefit' result comes from under-tuned graph models rather than from graph redundancy.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

3 major / 5 minor

Summary. The paper challenges the assumption that graph structure is necessary for good performance on common node-classification and link-prediction benchmarks. The authors tune a feature-only MLP on seven standard datasets (Amazon Computers, Amazon Photo, Coauthor CS, Coauthor Physics, Cora, CiteSeer, PubMed) and report that on five of them the tuned MLP nearly closes the gap with graph-based methods, implying that these five datasets are weak instruments for measuring graph-learning progress. They support this with feature-ablation studies showing that the MLP-GCN gap closes as node features are added, and they propose new benchmarks: a family of synthetic Watts-Strogatz link-prediction datasets plus three real-world link-prediction datasets where the MLP underperforms the GCN.

Significance. If the central claim is established, the paper has substantial value for the graph-learning community: it would show that several widely used benchmark datasets do not require graph structure, that under-tuned MLP baselines have distorted reported progress, and that new benchmarks are needed. The paper also ships code and synthetic datasets, which is a practical strength. However, the headline claim rests on an uncontrolled comparison between the authors' heavily tuned MLP and GNN numbers copied from prior papers, and the authors themselves concede in Section 7 that those GNNs were not tuned. The paper is therefore best read as a strong motivating study rather than as a definitive measurement of the benefit of graph structure.

major comments (3)
  1. [Section 4, Figure 1] The central claim that graph structure adds little on five of seven datasets is read off Tables 1 and 2, but those tables compare the authors' tuned MLP (Bayesian sweeps, 5 trials) with GNN results copied from Liu et al. (2020), Hoang & Lee (2023), and Shirzad et al. (2023) without establishing that the splits, feature preprocessing, training/validation protocol, early stopping, and trial counts are identical. Section 7 explicitly states that the authors did not tune those graph models. As a controlled measurement of the benefit of graph structure, this comparison is therefore not sufficient. The issue is not hypothetical: on Amazon Computers, Exphormer (91.6±0.3) exceeds the tuned MLP (82.6±0.6) by 9.0 points, and on PubMed, ACM-Snowball-3 (91.4±0.4) exceeds the tuned MLP (86.8±0.4) by 4.6 points, so the unqualified statement that one gains little benefit is in direct tension with the paper's own tables. A retuning of the graph methods under the same pipeline, or at least a systematic verification of protocol equivalence, is required before the headline conclusion can be drawn.
  2. [Section 5, Table 3, Figure 2] The feature study is interpreted as demonstrating that node features 'leak' graph information, but the observed closing of the MLP-GCN gap has plausible alternative explanations that are not controlled for: more features may simply make the classification task easier for both models, or may interact differently with optimization and capacity even when hyperparameters are tuned per dataset. The paper's causal claim that the benefit the GCN derives from the graph is 'also enjoyed by the MLP with a higher number of features' is an interpretation, not a measurement. The Cora negative control is useful, but it does not by itself rule out task-difficulty or optimization explanations for the Amazon Computers trend. The authors should either strengthen the causal evidence or restate the feature study as a correlation that is consistent with their hypothesis.
  3. [Section 7] The synthetic benchmark evidence is presented as showing that the WS1000 family separates MLP and GCN, but the numbers are thin. For WS1000, the GCN achieves 54.7±0.4 ROC AUC versus the MLP's 49.1±2.2, which is a small absolute gap, and no other graph method is reported. In Figure 2, the claim that 'the MLP begins to outperform the GCN' for increasing γ compares the MLP at γ>0 against the GCN at γ=0 only; the GCN is not retuned for γ>0, so the comparison does not establish how the graph method behaves on the harder variants of the family. This weakens the proposal that the parametric family provides a controlled way to benchmark graph methods.
minor comments (5)
  1. [Abstract; Section 3] The abstract says 'one gains little benefit from using graph structure on five datasets,' but the data in Tables 1 and 2 show several graph methods outperforming the tuned MLP by 4-9 points on those same five datasets (e.g., Exphormer on Amazon Computers and ACM-Snowball-3 on PubMed). The wording should be qualified to 'most previously reported, untuned graph methods' rather than a blanket 'little benefit' claim.
  2. [Appendix A] The Coauthor CS feature study says the datasets 'share the original graph from Coauthor Physics' when it should presumably say 'Coauthor CS'; please correct this typo.
  3. [Table 3] The parenthetical that MLP performance 'can be worse than random due to poor seeds' is vague and reads as an excuse rather than an explanation; it would be clearer to report the seed-dependent behavior separately or to use a variance-reduced evaluation.
  4. [Section 6, Table 4] For the three suggested real-world link-prediction benchmarks, only the GCN is compared against the MLP; reporting at least one or two additional graph methods would make the claim that these are suitable benchmarks more robust.
  5. [Section 4, footnote 3] Footnote 3 notes that the authors' retuned GCN exceeds the GCN numbers copied from Liu et al. (2020); this is an important caveat and should be given more prominence, since it illustrates that the graph-method numbers used in Tables 1 and 2 are not state-of-the-art even for the same architecture.

Circularity Check

0 steps flagged · score 0.0 of 10

No load-bearing circularity: the MLP-vs-GNN comparisons and feature/synthetic studies are empirical measurements, not derivations from their own conclusions.

full rationale

This is an empirical benchmarking paper. The central claim—that a well-tuned feature-only MLP matches or nearly matches graph methods on five of seven datasets—is a measurement: the tuned MLP numbers come from the authors' own DGL-based tuning pipeline, while the GNN numbers are imported from cited prior work. Neither quantity is defined in terms of the other, and no fitted parameter is renamed as a prediction. The feature study measures MLP and GCN accuracy on constructed feature subsets of the original graphs; this is an experiment designed to test a leakage hypothesis, not a derivation that assumes the conclusion. The synthetic WS1000 datasets are generated from a declared procedure with i.i.d. features independent of graph structure, so the GCN advantage there follows from the construction, which is an intentional benchmark design rather than circular reasoning. The only self-citation, Katsman & Gilbert (2024), appears as background in related work and as a similarity note for the synthetic feature-generation procedure; it is not load-bearing for the paper's empirical comparisons. The lack of a controlled retuning of the prior GNN baselines is a genuine methodological limitation affecting the strength of the headline comparison, but it is a validity concern, not circularity: the conclusion does not reduce to its inputs by definition, and the paper explicitly acknowledges that it did not tune those models.

Assumptions & free parameters 3 free parameters · 4 assumptions · 1 invented entities

The paper carries no derivational free parameters; its empirical claims rest on tuned model hyperparameters and on generation parameters for the proposed synthetic benchmarks. The load-bearing domain assumptions are split compatibility with prior papers and the meaningfulness of the feature-truncation ablation. One explanatory construct, graph-information leakage, is introduced without independent measurement.

free parameters (3)
  • MLP hyperparameters (layers, hidden size, learning rate, weight decay, dropout) = not reported in main text; example sweep file referenced in Appendix C
    The headline MLP accuracies in Tables 1 and 2 are produced by Bayesian sweeps; these choices determine the central comparison and are not fully specified in the text.
  • GCN hyperparameters for feature study and link prediction = not reported
    The GCN curves in Figures 1 and 3 and the link-prediction numbers in Table 4 come from the authors' own tuning; they set the measured gap between MLP and graph method.
  • Synthetic benchmark generation parameters (N, K, beta, gamma, nu) = N=1000, K=4, beta=0.5, nu=1, gamma in {0.2k for k in [5]}
    Chosen by hand to construct WS1000 and WS1000gamma; they define the proposed benchmarks but are not fitted to an external target.
assumptions (4)
  • domain assumption The DGL versions of the seven datasets use splits and preprocessing compatible with the prior-paper results cited in Tables 1 and 2.
    The 'little benefit from graph structure' conclusion compares the authors' MLP to numbers copied from Liu et al. (2020), Hoang and Lee (2023), and Shirzad et al. (2023). If splits, preprocessing, or trial counts differ, the gap is not a controlled comparison. Invoked in Section 3 and acknowledged in Section 7.
  • domain assumption Truncating each dataset's feature vector to the first k features produces a meaningful feature-poor to feature-rich spectrum.
    The feature study in Section 4 and Appendix A forms datasets such as Amazon Computers-k and Cora-k by taking the first k features in stored order. If feature order correlates with informativeness, the observed gap closure could be an artifact of ordering.
  • ad hoc to paper The closing accuracy gap as features increase is caused by node features encoding graph structure, not by increased MLP capacity, optimization ease, or feature-noise dilution.
    The paper 'posits' this explanation in Section 4 and uses it to interpret the gap; no independent measure of graph information in features is provided.
  • standard math Standard supervised learning and GNN machinery (backpropagation, message passing, DGL implementations) behave as described in the cited literature.
    Background used without proof.
invented entities (1)
  • WS1000 and WS1000gamma synthetic graph datasets
    purpose: Proposed as hard, graph-dependent link-prediction benchmarks that separate feature-only MLPs from graph-based methods.
    Newly constructed datasets described in Section 5 and Appendix B. They have no external validation yet, so whether performance on them tracks practical graph-learning progress is unverified.

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Cite this review

Pith. "Pith review of Revisiting the Necessity of Graph Learning and Common Graph Benchmarks." pith.science (2026). https://pith.science/paper/PQGXPSKM

@misc{pith2026241206173,
  author       = {Pith},
  title        = {Pith review of: Revisiting the Necessity of Graph Learning and Common Graph Benchmarks},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/PQGXPSKM}},
  note         = {Machine review of arXiv:2412.06173}
}
read the original abstract

Graph machine learning has enjoyed a meteoric rise in popularity since the introduction of deep learning in graph contexts. This is no surprise due to the ubiquity of graph data in large scale industrial settings. Tacitly assumed in all graph learning tasks is the separation of the graph structure and node features: node features strictly encode individual data while the graph structure consists only of pairwise interactions. The driving belief is that node features are (by themselves) insufficient for these tasks, so benchmark performance accurately reflects improvements in graph learning. In our paper, we challenge this orthodoxy by showing that, surprisingly, node features are oftentimes more-than-sufficient for many common graph benchmarks, breaking this critical assumption. When comparing against a well-tuned feature-only MLP baseline on seven of the most commonly used graph learning datasets, one gains little benefit from using graph structure on five datasets. We posit that these datasets do not benefit considerably from graph learning because the features themselves already contain enough graph information to obviate or substantially reduce the need for the graph. To illustrate this point, we perform a feature study on these datasets and show how the features are responsible for closing the gap between MLP and graph-method performance. Further, in service of introducing better empirical measures of progress for graph neural networks, we present a challenging parametric family of principled synthetic datasets that necessitate graph information for nontrivial performance. Lastly, we section out a subset of real-world datasets that are not trivially solved by an MLP and hence serve as reasonable benchmarks for graph neural networks.

Figures

Figures reproduced from arXiv: 2412.06173 by the authors.

Figure 1
Figure 1. We conduct a feature study on the Amazon Computers and Cora datasets by synthesizing datasets [PITH_FULL_IMAGE:figures/full_fig_p006_1.png] view at source ↗
Figure 2
Figure 2. Introducing parental dependence in node features very quickly leads the MLP to improve on link prediction. Each data point is obtained by tuning the MLP on the relevant synthetic W S1000γ dataset. The average of 5 trials is reported and the error region specifies one standard deviation. Synthetic Watts-Strogatz dataset Notice that the above class of graph datasets is very simple because the features are all drawn i.… view at source ↗
Figure 3
Figure 3. We conduct feature studies on the Amazon Photo, Pubmed, Coauthor Physics, Coauthor CS, and [PITH_FULL_IMAGE:figures/full_fig_p015_3.png] view at source ↗

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    " write newline "" before.all 'output.state := FUNCTION n.dashify 't := "" t empty not t #1 #1 substring "-" = t #1 #2 substring "--" = not "--" * t #2 global.max substring 't := t #1 #1 substring "-" = "-" * t #2 global.max substring 't := while if t #1 #1 substring * t #2 gl...

Pith tools

Reviewed August 11, 2026 · model on record in the stance chip above.