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Under review as a conference paper at ICLR 2027

What Does Graph Construction Preserve? A Discrete Ricci Curvature Diagnostic for Point Cloud Graphs

Abstract

Graph representation learning is a powerful general method for learning encodings for complex data, but the impact of graph construction methods on learning tasks remains understudied. Understanding how a graph construction method extracts particular data properties is important both for our understanding of what properties of the problem contribute to model performance, and to further improve downstream model performance. In this work we propose a diagnostic separation score—the Wasserstein-1 distance between discrete Ricci curvature distributions of labeled populations—to evaluate graph constructions. This diagnostic is training-free, and exposes some properties preserved by graph construction methods. We evaluate this diagnostic in the context of two application domains: quantum chemistry (the QM9 dataset) and collider physics (the JetSet dataset). On QM9, where bonds are known, separation based on the Ollivier-Ricci variant of discrete curvature tracks bond-recovery F1 across 19 constructions (Spearman ) without seeing the bonds and favors the  \AA radius graph construction, whereas separation based on the Forman-Ricci variant does not. On JetSet, which have no ground truth, all construction methods separate the flavors, but once we control for the number of nodes in the graph, only the radius graph construction method keeps most of its separation over all nodes. In addition to the diagnostic, we also measure an incremental predictive value of curvature as a model input: on QM9, a model gains most on the \AA graph teh diagnostic selects, whereas on jets curvature adds at most AUROC to a mean aggregating GNN. However, this gain is mostly matched by using a simpler feature, namely, the node degree.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Graph Construction, Discrete Ricci Curvature, Point clouds, Molecular graphs, Jet tagging

Reviews

Among:
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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_U2JpOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
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Paper summary

This paper studies how to evaluate graph construction methods for point clouds. The authors propose a training-free diagnostic that compares graph construction methods using the Wasserstein-1 distance between discrete Ricci curvature distributions of labeled populations. They compute this distance within bins defined by point count and composition and use complete graphs as a control.

The authors evaluate the diagnostic on QM9 and JetSet and compare model performance with and without curvature features. On QM9, Ollivier-Ricci (ORC) separation between hydrogen and heavy atoms correlates strongly with bond-recovery quality, whereas Forman-Ricci (FRC) separation does not show this correlation. On JetSet, radius graphs retain substantial ORC separation after controlling for point count and composition. In the QM9 prediction experiments, the construction selected by the diagnostic also yields the largest gains from curvature features. On JetSet, separation does not show a consistent association with gains from curvature features in the GNN and transformer.

Critical strengths
  1. The paper proposes a diagnostic for graph construction that requires no downstream model training and tests it against known physical structure. On QM9, ORC separation between hydrogen and heavy atoms uses only element labels and the constructed graph, without accessing the true bonds, yet correlates strongly with bond-recovery F1 across 19 constructions (Spearman ρ = 0.88, or 0.87 excluding the complete graph; Table 9). This independent reference provides initial support for a practical tool to assess graph constructions in small scientific point clouds before model training.

  2. By comparing different constructions of the same point clouds, the paper shows how edge-building rules affect the class differences detected by curvature. On JetSet, using ORC distributions pooled over all nodes and conditioning on total track count and secondary-vertex track count, the default radius graph retains a separation ratio of 0.68. The default kNN and unique-3 constructions retain 0.33 and 0.34, respectively, close to the complete graph's 0.38 (Figure 2a). This comparison offers a concrete interpretation of construction behavior: some curvature signals largely follow point count, while others continue to distinguish labeled populations after conditioning. It provides useful empirical insight into which data characteristics different construction rules emphasize.

Critical weaknesses
  1. The scope of applicability needs clearer support.

    The paper proposes using curvature separation to choose graph constructions and their parameters without training a model, but tests the diagnostic only on QM9 and JetSet. Both applications are useful, but it is unclear which properties of a new dataset would make the score a reliable guide. When should greater separation indicate better preservation of the structure relevant to the task? The paper discusses some domain-specific limitations, but does not give clear guidance on when this criterion should be used for other small scientific point clouds.

  2. The benefit of conditioning for construction choice is not sufficiently tested.

    QM9 provides a reference bond graph, but the main validation uses unconditioned separation (as in Table 9). Both atom populations come from the same molecules, and conditioning on size changes the per-molecule-mean scores by less than 3%, except near the estimation bias floor (Sec 5.1). The correlation supports agreement with bonding structure, but this setting does little to test the benefit of conditioning under substantial size confounding.

    JetSet has size confounding but no reference graph. The radius graph gives the best mean GNN baseline performance among the default sparse constructions on b-versus-light, which is encouraging. However, jointly conditioned ORC separation correlates only weakly with GNN baseline performance (Spearman ρ = 0.23, pooling within-task ranks over nine sparse defaults and three tasks; Appendix G.8). Model performance is only an indirect check of structural preservation. The complete-graph control shows that conditioning suppresses a pure size signal, but does not test whether the conditioned ranking agrees with independently known structure when size and structural differences coexist.

  3. Node–edge misalignment in the GNN implementation calls the predictive evidence into question.

    In utils/diminishing_returns_deep_models.py, build_padded_tensors sorts rows only by graph ID and fills the feature tensor by row position (lines 23–40), without ensuring that within-graph node order matches the original node indices. Meanwhile, build_padded_edges retains the original src/dst indices (lines 79–94), which SimpleGNN.forward uses directly to retrieve node features (lines 160–167). When sorting changes the within-graph node order, message passing can therefore connect features belonging to unintended node pairs. Until node–edge correspondence in the reported experiments is established, the GNN comparisons across constructions and the gains from curvature features remain difficult to interpret as reliable evidence about the intended graph constructions.

Questions for authors
  1. What guidance do the current results provide for deciding when curvature separation is a useful criterion for choosing a graph construction?

  2. Beyond the observed label separation, what evidence supports interpreting higher conditioned ORC separation as better preservation of task-relevant structure on JetSet?

4 comments
AuthorsOpenReview ↗

Response to Reviewer U2Jp: scope, conditioning tests, and the node-edge fix

The scope of applicability needs clearer support.

What guidance do the current results provide for deciding when curvature separation is a useful criterion for choosing a graph construction?

Weakness 1 and Question 1. We stated when the score is a reliable guide (Section 3.2). The labeled populations must differ in local connectivity in the true structure, each bin must hold enough point clouds, and parameters must be compared within one family of constructions. We added a six-step procedure for a new dataset (Appendix D.1). The procedure tests the assumption itself, because the fully connected graph must not exceed its permutation null and at least one construction must.

QM9 provides a reference bond graph, but the main validation uses unconditioned separation (as in Table 9).

Weakness 2, QM9. We tested the size control where a size difference and a reference graph coexist. We induced the size difference on QM9 by keeping hydrogens mostly from large molecules and heavy atoms mostly from small ones, and we left the bonds unchanged. Without size control, the fully connected graph separates the two populations and the Spearman ρ\rho with bond recovery falls from 0.88 to 0.81. Conditioning on molecule size returns both to their control values. Conditioning on a variable that does not carry the size difference does not restore the agreement (0.83). These results are in Section 5.2 and Appendix G.3.

JetSet has size confounding but no reference graph.

Beyond the observed label separation, what evidence supports interpreting higher conditioned ORC separation as better preservation of task-relevant structure on JetSet?

Weakness 2, JetSet, and Question 2. We added independent structural evidence on jets. JetSet records the decay vertex of each track, so we scored the edges of each construction against same-vertex track pairs, which the diagnostic never uses. Conditioned ORC separation tracks this recovery across the 36 constructions (ρ\rho = 0.60 overall, and 0.58, 0.44, and 0.72 within bb, cc, and τ\tau jets). The unconditioned separation, which uses no vertex information, agrees as well (ρ\rho = 0.66). On jets the benefit of conditioning shows in the permutation null, where the fully connected graph and most constructions no longer exceed chance once size is fixed (Section 5.2). These results are in Section 5.1, Figure 2b, and Appendix G.4. We agree that model performance is only an indirect check. With the corrected GNN, the correlation between conditioned ORC separation and the GNN baseline is 0.34 across the nine sparse default constructions and three tasks, and we report it as an observation (Appendix H.8).

Node–edge misalignment in the GNN implementation calls the predictive evidence into question.

Weakness 3. We confirmed the node-edge misalignment. The node table was sorted with an unstable sort while the edge index kept the original node positions. We fixed the sort with a stable one and added an alignment check that runs before training. The diagnostic, the QM9 control, and the transformer results are not affected. The corrected GNN runs are ongoing. So far we replaced the GNN results for the 12 default jet constructions, for 18 sweep constructions on bb vs light, and for 15 of the 22 QM9 constructions (14 for the dipole moment), and the remaining cells are marked as pending. Among the finished QM9 runs, the corrected GNN is most accurate on the graph that the diagnostic selects (0.0082 Ha). We withheld the claims that rested on the GNN degree control until its rerun finishes, and we will update the paper when the runs complete.

Thank you for the response. I maintain my score for the following reasons: (1) the bug fix changes the GNN results substantially (e.g., the radius-graph baseline falls from best to second-lowest), which the response does not discuss; (2) on JetSet, the pooled and per-flavour results disagree on whether conditioning helps; (3) singling out the radius family relies on a cross-family comparison, which the paper itself calls less reliable.

AuthorsOpenReview ↗

Follow-up to Reviewer U2Jp (1/2)

Thank you for your follow-up comments. We address the three points as follows.

the bug fix changes the GNN results substantially (e.g., the radius-graph baseline falls from best to second-lowest), which the response does not discuss

You are correct that our first response did not discuss how the bug fix changed the GNN results. The corrected runs were still in progress at the time, and we did not want to describe the change from partial results. All reruns are now complete, and every GNN entry that the bug could affect comes from the corrected code.

Three GNN results on jets changed:

  • The GNN baseline no longer favors the radius graph. On b vs light, the corrected GNN's AUROC without curvature on the radius graph is 0.7192. The value 0.7192 is the second lowest among the sparse default constructions, which range from 0.7140 to 0.7247. We withdrew the claim that the GNN baseline on jets follows the diagnostic. The paper now states that the GNN's accuracy without curvature is nearly the same on every construction.
  • The gains from curvature are smaller. On b vs light, curvature improves the GNN's AUROC by only +0.0007 to +0.0075, depending on the construction. On τ\tau vs light, curvature lowers the GNN's AUROC significantly on eight of the ten sparse default constructions that enforce a minimum degree.
  • The degree control experiment is complete. In the degree control experiment, we gave the GNN each node's degree in place of the node's curvature. Node degree alone recovers half or more of the curvature gain on all eight constructions that we tested. On the radius graph, the two gains are almost equal: +0.0101 from degree and +0.0098 from curvature. The degree control result confirms what the initial submission reported, namely that node degree mostly matches the curvature gain. We do not claim that curvature gives the GNN information beyond node degree on jets.

The diagnostic itself did not change. The separation scores and the transformer results do not involve the GNN, so the separation scores and the transformer results are identical to the results in the original submission. The permutation nulls and the vertex recovery test, which we added in the first revision, also do not involve the GNN, so the bug fix did not affect them either.

On QM9, where a reference graph exists, the bug fix brought the GNN into agreement with the diagnostic. In the original submission, the GNN's error without curvature on the 1.8 \AA\ graph was 0.0219 Ha, which was higher than the GNN's error on the fully connected graph (0.0159 Ha). With the corrected code, the GNN's error on the 1.8 Å graph is 0.0082 Ha, which is the lowest error among all 22 constructions.

The model results therefore support the diagnostic on QM9 but not on jets.

  • On QM9, the GNN is most accurate, and the transformer gains most from curvature, on the graph that the diagnostic selects.
  • On jets, the models gain about as much from curvature on the fully connected graph, which has no structure, as on the radius graph that the diagnostic selects. A model's gain therefore cannot tell us which construction is better.

For this reason, we compare constructions on jets by conditioned separation and not by model gain.

AuthorsOpenReview ↗

Follow-up to Reviewer U2Jp (2/2)

This comment continues our reply:

on JetSet, the pooled and per-flavour results disagree on whether conditioning helps

You are correct that the pooled and per-flavor results disagree. The table below gives the Spearman correlation, across the 36 constructions, between a construction's separation and the construction's same-vertex F1. The same-vertex F1 measures how well the edges of a construction match the pairs of tracks that come from the same decay vertex (Appendix G.4).

JetsWith conditioningWithout conditioning
Three flavor pairs pooled0.600.66
b vs light0.580.51
c vs light0.440.27
τ\tau vs light0.720.66

Pooled, conditioning lowers the correlation slightly (0.66 to 0.60). Per flavor, conditioning raises the correlation. With only 36 constructions, neither change is large enough to be meaningful, so we do not claim that conditioning improves the correlation with same-vertex F1.

The table shows that constructions with a higher separation also connect more of the track pairs that come from the same decay vertex, with or without conditioning on jet size. Every correlation in the table is positive, and the pooled correlation with conditioning (0.60) has a 95% bootstrap interval of [0.31, 0.80]. When we replace curvature with node degree or triangle count and compute the separation in the same way, the correlations with same-vertex F1 are negative (−0.57 and −0.59).

We condition for a different reason. Jet flavors differ in the number of tracks per jet, and curvature depends on the number of tracks. Without conditioning, two flavors can therefore look different even on a graph with no structure. Conditioning compares only jets of the same size. Two tests show that conditioning removes the size effect.

On jets, the fully connected graph has no structure, yet without conditioning the fully connected graph separates the flavors. With conditioning, 0.38 of the fully connected graph's separation remains, which is the same fraction that remains when the flavor labels are shuffled (0.38).

On QM9, the bonds are known. When we induce a size difference between the two populations, the correlation between separation and bond recovery falls from 0.88 to 0.81. Conditioning restores the correlation to 0.88.

singling out the radius family relies on a cross-family comparison, which the paper itself calls less reliable

Our earlier wording made the selection of the radius family unclear, and we thank you for identifying the problem.

To be precise about terms: a family is a construction rule, such as kNN or the radius graph, and a construction is a family with one parameter setting, such as the radius graph at ϵ\epsilon = 0.3.

We do not select the radius family by comparing raw scores across families. We select the radius family because the radius graphs are the only constructions that stay well above their own shuffled-label baseline.

For each construction we compute two numbers: the fraction of the construction's separation that survives conditioning, and the same fraction when the flavor labels are shuffled. The paper calls the difference the excess (step 5 of Appendix D.1, and the "excess" column of Table 2a). Three examples:

ConstructionSurvives conditioningWith shuffled labelsExcess
Radius graph (ϵ\epsilon = 0.3)0.680.380.30
Laman graph0.390.380.01
Fully connected graph0.380.380.00

Across all 36 constructions, the four radius graphs have an excess of 0.19 to 0.38. The largest excess for any other construction is 0.03 (Section 5.2, Table 2a).

The excess can be compared across families because both numbers are fractions of the construction's own separation. The procedure in Appendix D.1 now states this explicitly.

The within-family restriction that you mention applies to a different step. Step 6 of the procedure compares conditioned separations within one family in order to choose a parameter. Step 5, which computes the excess, tests each construction only against the construction's own shuffled labels.

The vertex recovery test that we added in response to your review ("does not test whether the conditioned ranking agrees with independently known structure") points to the same family. The construction with the highest same-vertex F1 is the radius graph at ϵ\epsilon = 0.2, and the same construction has the largest conditioned separation among all 36 constructions (Section 5.1, Figure 2b, Appendix G.4).

We do not compare the remaining families with one another. We reworded the limitation in Section 6 to state that the raw scores, and not the shuffled-label test, are less comparable across families.

Thank you again for the careful reading. These points made the paper more precise about what it does and does not claim.

Reviewer_AhHxOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This work studies how to evaluate graph construction quality from point-cloud data. Given a constructed graph with node labels, they propose population separability, which uses Wasserstein distances between the curvature distributions of all node categories. Experiments on QM9 and JetSet shows that this separability is positively correlated with ground-truth edge recovery, and the curvature feature can also be incorporated into prediction model to improve the downstream performance.

Critical strengths
  • The paper addresses an interesting and relevant question: how to assess graph construction quality in a training-free manner.

  • Substantial empirical study over different graph construction approches, with bond-recovery controls, size and composition conditioning, and degree-feature ablations. The proposed separation score is demonstrated to be positively correlated to true bound recovery.

Critical weaknesses
  • The paper lacks comparisons with simpler diagnostics, perhaps such as separation scores based on degree, triangle or other motif histogram. It therefore remains unclear whether curvature offers an advantage over other evaluation alternatives.

  • The diagnostic requires predefined node labels, so it is not applicable when no meaningful node labels is available.

  • Moreover, interpreting higher separation as better graph construction seems to implicitly assume that the underying edge connectivity produces greater curvature differences between the node categories. The authors may discuss what assumptions that make it hold and if there are real-world graphs that could violate it.

Questions for authors

See Weeknesses.

1 comment
AuthorsOpenReview ↗

Response to Reviewer AhHx

Thank you for your comments. We are glad that you found the question interesting and relevant (assessing a graph construction without training), the empirical study substantial, and the score positively correlated with true bond recovery. We addressed each of the three points with new results or new text.

The paper lacks comparisons with simpler diagnostics, perhaps such as separation scores based on degree, triangle or other motif histogram.

We added the comparison with simpler diagnostics (Section 5.2, paragraph "Simple descriptors", Appendix G.13). We scored node degree, triangle count, and the clustering coefficient through the same pipeline as curvature on both datasets, and we compared all five descriptors by their agreement with a true structure that none of them is given. Table 2b gives the Spearman ρ\rho with bond recovery on QM9 and with same-vertex recovery on jets.

ORCclusteringFRCdegreetriangles
QM9 (19 constructions)+0.88+0.60+0.09−0.32−0.60
Jets (36 constructions)+0.60+0.43−0.29−0.57−0.59

The separation of degree and of triangle count correlates negatively with recovery of the true structure in both domains, and clustering agrees with the true structure more weakly than ORC does. Degree and triangle count exceed their own permutation nulls on more constructions than ORC does on jets (24 and 22 against 9). The jet flavors therefore do differ in degree, but that difference does not agree with vertex recovery.

The diagnostic requires predefined node labels, so it is not applicable when no meaningful node labels is available.

We agree that the diagnostic needs labels, and we now state this as a limitation (Section 6, Limitations, "Requirements"). We also explain why the requirement is modest (Section 1, Appendix D.1). The class label of the supervised task is sufficient, because every point takes the label of its point cloud, as each track takes the flavor of its jet. A per-point attribute that is already in the data, such as the element of an atom, is also sufficient.

Moreover, interpreting higher separation as better graph construction seems to implicitly assume that the underying edge connectivity produces greater curvature differences between the node categories.

We stated the assumption behind interpreting higher separation as better preservation (Section 3.2, paragraph "When does higher separation mean better preservation?"). The two labeled populations must differ in local connectivity in the true structure, as hydrogens with one bond and heavy atoms with several do.

The authors may discuss what assumptions that make it hold and if there are real-world graphs that could violate it.

Real data can violate this assumption, and the permutation null is how a user detects the violation. The permutation null is the separation obtained after shuffling the labels in a way that keeps the size of every point cloud fixed, repeated 200 times. We treat the separation of a construction as evidence of preserved structure only if it exceeds all 200 shuffled values. The assumption fails when the label does not depend on which points are connected. One example is the sign of a track's electric charge. Positive and negative tracks come from the same decay vertices, so the true structure gives the two populations the same local connectivity. For a label of this type we expect no construction to exceed its permutation null, and the procedure then reports that the label cannot be used, instead of selecting a construction (Appendix D.1, step 5). We did not run the charge label. The case we did run is the label shuffle itself, which removes the relation between label and connectivity by design. Under the shuffle the separation of every construction falls to the null level (Figure 1, Section 3.2).

We also tested the score against structure that is never an input to the score. The chemical bonds on QM9 and the decay vertices on jets are not used to build any graph or to compute the score. We use them only afterward, to check whether constructions with higher separation recover more of that structure. They do, with ρ\rho = 0.88 on QM9 and 0.60 on jets (Figure 2).

Finally, we clarified the role of the predictive results. We treat the gain from curvature as a secondary check. The gain follows the diagnostic on QM9 but not on jets, where curvature from the fully connected graph gives about the same gain (Section 5.3, Table 3).

Reviewer_nvS8OpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The authors aim to study how curvature distribution in a graph separates labels for various graph constructions and if concatenating curvature as in input helps downstream. The authors use just 2 datasets, one for molecules the other on sprays of particules in collisions, to reach their general claims, being that discrete Ricci curvatures actually do not compute structure accurately and are biased by size, and that just node degrees are probably just as informative if not more than curvature.

Critical strengths
  • The authors ask some simple questions, especially Q1 and Q3: does curvature allow to separate labels and does concatenating curvature improve downstream performance? Simple is good.

  • The authors provide 57 pages of appendix, which could please those interested in the micro-details and results on the work.

Critical weaknesses
  • In my opinion, the paper is not readable or understandable for the general AI community, which is the audience of this venue. A major problem is that the authors focus exclusively on the QM9 and jets datasets, involving two completely different and non-standard datasets in general AI, and the authors poorly help the reader to understand the setting on these data. If the paper is not understandable for the general audience of the venue, then I cannot recommend it for acceptance. Perhaps it would be of high interest for very specific audiences for which these settings are well-known and natural. In that case, I encourage the authors to consider alternative venues targetting these specific readers. If the authors want to target the general AI audience, then I encourage the authors to write a paper with them in mind. In particular, clear explanations of the problems are highly needed. These can come with better textual descriptions, but would be most improved with figures illustrating concepts (figures are crucially missing from the main manuscript, to illustrate the data, the tasks, the methodology, and other issues...).

  • What is truly upsetting is that the authors do ask questions that are of interest to the general AI community, but the answer and the methodology to reach those answers are not. I highly encourage the authors to also include much more standard settings (and only 2 datasets falls far short from anything meaningful to claim anything general). Since they are mostly targetting classification in graphs, why not just work on mainstream graph classification settings? There are so many types of graphs to choose from (recommendation systems, social networks, citation graphs...) that are so much simpler to understand and would give much more general insight in order to claim a general response to the general claims.

  • The authors failed to motivate why the paper should actually exist. 1) Did I learn anything important after reading the submission? No. 2) Is the submission useful in practice? Again no, and this is perhaps best summarised by the authors themselves in the last sentence of the abstract: "However, this [curvature] gain is mostly matching by using a simpler feature, namely, the node feature" and at the end of the introduction l118 "[The diagnostic] measures what a construction preserves, not a model with do with it". There is always a risk of falling short when providing a diagnostic-only submission, without actually showing how it can be truly beneficial downstream. I believe this work falls in this category.

  • In general, I am not claiming the submission is void of content, knowledge, or good science. However, I believe the authors absolutely need to heavily rework their presentation so that this can become more apparent and more digestible by the community of the venue the work has been submitted to.

  • A few things to help the authors improve their submission:

    • Simplify the experimental settings and use common ones in the community. As the motivating questions are simple and general, they can be studied anywhere and not only in super niche settings. Diversify the datasets and graphs to show general (or random) behaviours.
    • Try to find or better motivate downstream use by practitioners.
    • Provide many illustrations to boost readability.
    • Study 2D/3D graphs: 2D/3D pointclouds are highly visual and common (eg in curve and shape analysis). The advantage there is that the manifold is intuitive and visible by everyone from the point cloud alone, the curvature can be geometrically computed (and not just from the graph topology) to correctly approximate the actual manifold Gaussian curvature. 2D/3D experiments also provide fundamental sanity checks. As high-dimensional manifolds are incomprehensible, any output in high-dimension can be ok, whereas this is not true for 2D/3D where incorrect visual results become obvious even if score metrics can be ok. I would encourage to show that in 2D/3D the diagnosis provides something intuitive, expected, and correct, because if it does not then for sure in cursed high-dimensions (where most graphs lie) then for sure it will not.
    • The authors only considered undirected graphs (l141), yet directed graphs are also of high interest and very common. The authors might want to explore studying directed graphs without undirecting them (which leads to Finsler geometry rather than Riemannian geometry).
    • The authors use the Euclidean distance as distance measure between points (l142). While this is very common, it is only done for nearby points. The distance between far away points should instead be given geodesically. Also, the Euclidean distance is unreliable, even for points embedded closely, as the underlying geodesic manifold distance can be very large even for close points (for example a hand in resting position is close to the hip yet it is very far from it geodesically on the human body). In general, it could be of interest to consider other distance measures, or even other embedding spaces where distances are computed (Euclidean distances on latents rather than raw inputs).
    • The authors list some graph constructions. Several of them are universal (kNN, radius-based, fully connected), others are much less common (2 graphs from the recent work Araz et al. from this year 2026). It would be worthwhile to consider alternative graph constructions, if only to create more baselines than fully connected, such as random graphs (uniform random edges, which is not very realistic, or incrementally random edges with probability depeding on the degree, which is more realistic compared to real world graphs like social networks).
    • The authors focus on Ricci curvature, using 2 variants. Should they follow my recommendation to work on 2D/3D data, they can use Gaussian curvature, a much better curvature estimate that actually accounts for the geometry of the manifold and is not purely topological. It would be of interest to compare Ricci estimates vs proper curvature estimates and see what is lost in the process from the perspective of the diagnosis.
    • I understand that the authors work in the highly discrete setting, where graphs are essentially tiny (double digit number of nodes). Nevertheless, it would be of interest to explore or remind continuum/asymptotic limits and study the evolution from the very small regime all the way to the very high node/asymptotic regime. Is there a brutal transition phase or do behaviours change gradually? By solely studying the very low regime we are missing a large part of the picture.
    • The Δ\Delta-Performance measure is not satisfactory on its own. It is an interesting measure, giving the difference in performance downstream between augmenting the input with the curvature via concatenation and just using the raw input. However, finding positive gains in this metric cannot lead on their own to the conclusion that curvature is beneficial, or rather than curvature is THE beneficial concept to boost performance downstream. I believe other interesting Δ\Delta baselines should be studied. The degree could be one as claimed in the conclusion of the work. But more related to the curvature, I would encourage to study concatenating higher moments (as in momenet Joshep-Rivlin et al. 2019)
    • The results to answer Q3, which is an interesting question (does including explicitly curvature help downstream?), are dumped to the appendix (no table or figure in the main manuscript), and a large bunch of inline numbers are given in the text, making it hard to parse and get an overview of a global behaviour. I highly encourage to provide a compact presentation of results in the main manuscript for this question, either in the form of tables or figures (or both!). This would greatly boost readability and make the claims more convincing.
    • l459: To answer such a general question like "Does separation predict the gain", it is absolutely necessary to study more than just 2 datasets from niche fringe AI communities compared to general graph community.
    • l114: do not mix in the Introduction Section 1 the general setting of the work ("The two scores answer different questions") with the outcome of the Results ("on jets they disagree") of Section 5. This can be extended throughout the paper. I thus highly encourage to containerise better the sections, and it should drastically improve the readability of the work. Indeed, everything should be fairly straightforward and easily readable for the general audience up to maybe the description of the experiments on the non-standard datasets.
    • l30: teh --> the
    • l114 & l116: Two : in the same sentence.
    • l141 & l207: There seems to be a conflict with notations n and N.
    • l210: PV and SV are undefined at this point in the submission. In general, explain acronyms before they are used, this will help readability.
    • I did not review in detail the supplementary, which is much too long for a human reviewer to parse. From quickly scrolling through, a few things caught my attention:
      • There are formatting problems with tiny text that overlaps other text, eg in Table 15. -There are several huge tables, e.g. Table 22a (but also 24a, 32a, 34a, 36a...) with 22 lines and 6 columns, where all the numbers in the columns, including 95% percentile brackets, are absolutely identical across all lines! The only exception being the GNN column. I highly encourage the authors to check whether this is normal or a bug, and to perhaps explain systematically in the captions of the tables why these behaviours occur, especiall since in Table 22b, which is the same except now the input has curvature features, the numbers seem to change.

Joshep-Rivlin et al., Momenet: Flavor the Moments in Learning to Classify Shapes, ICCV-W, 2019

Questions for authors

See weaknesses above.

Perhaps the most important issue is to better motivate the existence of the work. Thus, questions could be: why does this diagnosis matter? What does it bring to the table that did not exist before? How is it useful in practice?

3 comments
AuthorsOpenReview ↗

Response to Reviwer nvS8

Thank you for your comments. We are glad that you found that "the authors do ask questions that are of interest to the general AI community" and that "Simple is good". We agree that the submission stated its limits more clearly than its use, and we reorganized the paper around the use.

The authors failed to motivate why the paper should actually exist.

We rewrote the motivation in the introduction. Every graph model on point clouds starts from a construction rule. The rule is usually a default taken from earlier work (for example, kk = 16 nearest neighbors for jets) or is tuned through a trained model, and there is usually no reference graph to check it against. Our diagnostic provides this check without training. On QM9 the diagnostic tracks bond recovery across 19 constructions (Spearman ρ\rho = 0.88) and selects the 1.8 \AA\ radius graph without any information about the bonds. Curvature from that graph reduces the error of a transformer on the HOMO-LUMO gap from 0.0180 to 0.0095 Ha. Among the 15 constructions whose corrected GNN runs finished, the GNN is also most accurate on that graph (0.0082 Ha, against 0.0104 Ha on the next best). We also show that on jets, curvature comparisons that do not control for size mostly measure point count (Section 5.2).

The two sentences that you quoted from the abstract and from line 118 are no longer in the paper. We withdrew the statement that node degree matches the gain, because it rested on the GNN degree control, which is being rerun after we fixed a node-order bug that Reviewer U2Jp found. The QM9 result above is the downstream evidence that you asked for.

In my opinion, the paper is not readable or understandable for the general AI community, which is the audience of this venue.

QM9 and jet tagging are established benchmarks at ICLR and ICML. Our paper cites a QM9 model published at ICLR 2020 (DimeNet) and a jet-tagging model published at ICML 2022 (Particle Transformer), and the ICLR call for papers lists "applications to physical sciences (physics, chemistry, biology, etc.)" among its topics. We agree that the submission did not explain the two settings well enough. We added a diagram of the pipeline (Figure 1), a dataset table that defines jet, track, and primary and secondary vertex (Table 1), a primer figure that shows each dataset from physical object to point cloud to labels (Figure 3), a figure of one molecule and one jet under the default graphs (Figure 4), and a six-step procedure (Appendix D.1).

only 2 datasets falls far short from anything meaningful to claim anything general

We clarified that our claims apply to small labeled point clouds that carry no edge information (Section 6, Limitations, "Scope"). We agree that two datasets is a small number, and we list other domains as untested. Citation and social network graphs are interesting, but in their standard form the edges are given and each dataset is a single large graph, not a set of small point clouds, so they are outside the setting we tested.

The results to answer Q3 [...] are dumped to the appendix

We reorganized the results by our findings and added a compact table of the gain results to the main text (Table 3). We also rewrote the introduction so that it states the problem, the diagnostic, and the contributions, and the detailed results are in Section 5.

I highly encourage the authors to check whether this is normal or a bug

The identical columns are expected and are not a bug. Without curvature features, five of the six models never see the graph, so their baseline is the same for every construction. We now report that baseline once per table. We also fixed the typos, the nn and NN notation, the acronyms, and the overlapping tables.

Study 2D/3D graphs

Both of our datasets are already point clouds of this kind. QM9 atoms are 3D positions, and jet tracks are 2D points given by their (Δη\Delta\eta, Δϕ\Delta\phi) offsets from the jet axis (Table 1, Figure 3). None of our graphs is built from high-dimensional coordinates, and Figure 1 illustrates each step on a 2D toy example.

The Δ\Delta-Performance measure is not satisfactory on its own.

We agree that a positive gain does not show that curvature is the concept that helps. The paper now states that the gain measures what a model fails to extract from its inputs (Appendix I), and we treat the gain as a secondary check. We did not run the moment features of Momenet. On the diagnostic side we added node degree, triangle count, and the clustering coefficient (Section 5.2, Appendix G.13).

The authors only considered undirected graphs (l141)

We did not study directed graphs, geodesic or learned distances, random-graph baselines, or the large-nn regime, and we now list these as limitations (Section 6). We did not use Gaussian curvature because it is a property of the points and is the same for every graph built on them, so it cannot distinguish graph constructions.

I thank the authors for their response.

It seems that a lot of things have changed in the revised submission, which I could not go through in detail as the changes are both so numerous and the submission is so long (92 pages!): text, tables, figures in the main manuscript and the appendix. It would have been nice to mark the changes in colour to help the reviewers see the exact differences.

Overall, the authors seem to have taken into account my difficult comments and I think they have substantially improved their submission. Most importantly, the paper now seems readable for a much wider audience, covering most of the ICLR community, with a completely revised presentation. The introduction section has been completely rewritten, and it to some extent better motivates the existence of the work.

Another very important aspect that was a major problem in the original version was the conclusion reached that essentially the proposed curvature diagnostic was not useful, and that just looking at node features was just as informative "However, this [curvature] gain is mostly matching by using a simpler feature, namely, the node feature". However, the authors have clarified that these conclusions were drawn based on buggy experiments and have withdrawn these conclusions. While I understand some experiments are still running to better understand what is going on, I am more satisfied regarding this aspect after the author response. Yet, given the prior existence of bugs and the non definitive conclusions, I cannot claim with certainty that the approach is in fact useful.

I still have an important concern regarding the fact that the authors only tackle 1) tiny graphs, and 2) evaluate on just 2 datasets. Regarding 1) tiny graphs, it would be nice to get the full picture on larger graphs, but I can understand, although not necessarily agree, if authors would prefer to focus on tiny ones fitting the studied scientific settings. My bigger concern is 2) the evaluation on just 2 datasets. The problem is that this work is at its core a diagnostic paper. It tries to answer general questions on (tiny) datasets, especially ranking which graph construction to use using Ricci curvature. But it is just not possible to reach general conclusion with just 2 datasets. Even if the work would solely cover the two settings tackled by the authors, more datasets would be necessary in those settings.

Given the fact that authors have substantially revised their work in what I believe to be a good direction, I have decided to raise my score. However, given the important remaining concerns, and some uncertainty still whether the work is really useful downstream, I am not confident enough to recommend acceptance. I will thus raise my score from 1 to 2.

AuthorsOpenReview ↗

Follow-up to Reviewer nvS8

Thank you for taking the time to read the revision carefully, and for raising your score. We appreciate it. Your comments on degree, downstream evidence, and the number of datasets led directly to changes in the introduction, Section 3.2, Section 5, and Section 6. These changes made the paper clearer.

the authors have clarified that these conclusions were drawn based on buggy experiments and have withdrawn these conclusions.

We need to correct our earlier statement about node degree. In our first response, we withdrew the statement that node degree matches the GNN's gain from curvature, because the experiment behind that statement was being rerun. The corrected experiment has now completed, and the corrected experiment confirms the statement: on jets, node degree alone recovers half or more of the GNN's gain from curvature. We want to be direct about this result, because your follow-up relied on the withdrawal. We do not claim that curvature gives the GNN information beyond node degree on jets.

The degree result does not make the diagnostic redundant. The degree result concerns curvature as a model input. The diagnostic uses curvature differently: the diagnostic scores a graph construction before any model is trained. For scoring a construction, degree is not a substitute for curvature. We scored degree the same way as curvature. The degree separation measure correlates negatively with the true structure in both domains (−0.32 on QM9 and −0.57 on jets), while the Ollivier-Ricci separation measure correlates positively (+0.88 and +0.60). These correlations do not involve the GNN and were not affected by the bug.

given the prior existence of bugs and the non definitive conclusions, I cannot claim with certainty that the approach is in fact useful.

All corrected experiments are now complete, so the conclusions in the revised paper are final. On QM9, curvature from the graph that the diagnostic selects reduces a transformer's error from 0.0180 to 0.0095 Ha, and the corrected GNN is most accurate on that graph. On jets, we do not claim a downstream benefit, because the models gain about as much from curvature on the fully connected graph, which has no structure, as on the radius graph that the diagnostic selects.

it is just not possible to reach general conclusion with just 2 datasets. Even if the work would solely cover the two settings tackled by the authors, more datasets would be necessary in those settings.

This is a fair point, and we agree that two datasets cannot support a general claim. Additional datasets are the natural next step, and we could not add one within the rebuttal period. The paper responds in two ways instead. First, we limit the paper's claims to small labeled point clouds, and we list larger point clouds and other domains as untested in the limitations (Section 6). Second, we provide a six-step procedure for applying the diagnostic to a new dataset (Appendix D.1).

Comments on the paper

2 comments
AuthorsOpenReview ↗

Response to all reviewers: new checks, presentation changes, and status of the GNN reruns

We thank the three reviewers for their careful reading and constructive feedback. The reviewers found that the paper asks an interesting and relevant question (AhHx) that is of interest to the general AI community (nvS8), that the diagnostic needs no training and is tested against known physical structure, with ρ\rho = 0.88 against bond recovery on QM9 (U2Jp, AhHx), that the empirical study is substantial (AhHx), and that the comparison of constructions shows which characteristics of the data each construction rule emphasizes (U2Jp). We kept the method and the two datasets, and we added the checks that the reviews asked for.

We scored node degree, triangle count, and the clustering coefficient through the same pipeline as curvature on both datasets, each against its own permutation null, as Reviewer AhHx requested (Section 5.2, paragraph "Simple descriptors", Table 2b, Appendix G.13). We stated the assumption behind the score, the conditions under which the score is reliable, and a six-step procedure for a new dataset, as Reviewers U2Jp and AhHx requested (Section 3.2, Appendix D.1). We tested the size control against a known answer by inducing a size difference between the two populations on QM9, as Reviewer U2Jp requested (Section 5.2, Appendix G.3). We scored each jet construction against same-vertex track pairs from the simulation, which gives independent structure on jets, as Reviewer U2Jp requested (Section 5.1, Figure 2b, Appendix G.4).

We revised the presentation in response to Reviewer nvS8. We rewrote the motivation in the introduction, and we added a diagram of the pipeline (Figure 1), a dataset table that defines the terms of both domains (Table 1), a primer figure that shows each dataset from physical object to point cloud to labels (Figure 3), and a compact table of the gain results in the main text (Table 3). We also reorganized the results by finding.

The diagnostic and the transformer results do not depend on the GNN input code, so those results and their interpretation are unchanged. We fixed the node-order bug in the GNN input pipeline that Reviewer U2Jp found, and we verified the fix with an alignment check that runs before training. The corrected GNN runs are still in progress. We replaced the GNN results wherever a corrected run finished, and the remaining cells are marked as pending in the revised PDF. We will update it once all the runs complete.

AuthorsOpenReview ↗

Update: all corrected GNN runs are complete

We thank the reviewers for their patience. The revised paper now contains every corrected GNN result, and no tables have any pending results.

  • Results the GNN bug fix did not affect: The diagnostic, the recovery tests, the size-control test, and the transformer results do not involve the GNN, so the bug fix did not affect any of the four.
  • QM9: The corrected GNN is most accurate on the 1.8 \AA\ graph that the diagnostic selects (0.0082 Ha, compared with 0.0159 Ha on the fully connected graph). Adding curvature improves the corrected GNN's gap error on 21 of 22 constructions (Section 5.3, Appendix H.1).
  • Jets: The GNN's accuracy without curvature is nearly the same on every construction, and its gains from curvature are small (Section 5.3, Appendix H.2 to H.4). Node degree alone recovers half or more of those gains (Appendix H.6).

In our first responses, we withheld the statement that node degree matches the GNN's curvature gain while the degree control experiment was rerun. The corrected experiment confirms that statement, and the paper states it again (Section 5.3).

We compare constructions by conditioned separation, not by model gain. The paper states this explicitly at the end of Section 5.3 and in conclusion (iv) of Section 6.

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

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