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Under review as a conference paper at ICLR 2027

Benchmarking Reliability in Graph Representation Learning

Abstract

Graph representation learning (GRL) has evolved from topology-only graph embeddings to task-specific supervised GNNs and, more recently, to reusable representations and graph foundation models (GFMs). However, existing GRL benchmarks primarily evaluate clean-setting performance, transfer, adaptation, and task coverage, while reliability-relevant evaluations are typically conducted one axis at a time under different method pools and protocols. As a result, it remains unclear how modern GRL methods compare under matched conditions when deployment conditions affect graph signals, graph contexts, label support, structural groups, or predictive evidence. We introduce GRL-Reliability, a multi-axis benchmark for evaluating GRL reliability. GRL-Reliability evaluates twelve representative methods, spanning topology-only embeddings, supervised GNNs, self-supervised graph models, and GFMs, on twenty-five graph datasets under standardized evaluation conditions while preserving method-native adaptation where available. The benchmark covers five evaluation axes: corruption robustness, OOD generalization, class imbalance, fairness, and interpretation, with per-axis and subcondition reporting rather than a single aggregate score. Our analysis reveals three cross-axis insights. First, even tests that intervene on the same graph factor can produce distinct method profiles, showing that closely related tests capture different aspects of reliability. Second, foundation-era methods show axis-specific strengths rather than broad reliability advantages. Third, degree shift and rare-class coverage remain challenging across the evaluated method set, revealing deployment regimes where current GRL methods still have substantial room for improvement. The benchmark, evaluation protocols, and code are available at: https://anonymous.4open.science/r/GRL-Reliability-1889/.

Primary area:
datasets and benchmarks
Keywords:
Graph Representation Learning, Reliability Evaluation, Benchmarking

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_RNAQOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The authors propose GRL-Reliability, a multi-axis benchmark for evaluating Graph Representation Learning Reliability. They evaluate twelve representative methods, spanning topology-only embeddings, supervised GNNs, self-supervised graph models, and GFMs, on twenty-five graph datasets under standardized evaluation conditions.

Critical strengths

It's a benchmark paper and it correctly cover many graph learning methods with separate evaluations of relevant reliability risks. It correctly details protocols, statistical analysis, severity sweeps and make the results easy to access The paper also add an analysis on pretraining unseen graphs which is a useful check.

Critical weaknesses
  • Performance drops can give misleading robustness rankings. For instance on BACE, GraphSAGE has the smallest scaffold gap, yet OFA achieves substantially higher scaffold-test AUC (66.6 vs. 56.9). Even if absolute scores are reported, the cross-axis analysis ranks robustness using drops. This weakens the conclusion on model selection since smaller degradation does not necessarily mean better performance under deployment shifts.

  • The overlap in pertaining limits OOD evidence: The temporal and inductive-entity experiments use graphs included in pretraining, so downstream-held-out nodes or entities are not necessarily unseen during pretraining. The paper acknowledges this, but the unseen-graph analysis does not resolve it for these two scenarios. Consequently, these results provide limited evidence of generalization to genuinely unseen future data or entities.

Questions for authors
  • Do the cross-axis conclusions hold when robustness is ranked by absolute corrupted/OOD performance rather than performance drop?

  • Can the temporal and inductive-entity experiments exclude future nodes and held-out entities from pretraining?

  • How stable are the attribution rankings under another explainer, particularly one that scores edges directly?

  • Have you considered feature missingness beyond Gaussian noise on embeddings? Ferrini et al., “Rethinking GNNs and Missing Features: Challenges, Evaluation and a Robust Solution,” (ICML 2026) studies how missingness mechanisms affect robustness evaluation. Discussing this connection would help clarify which deployment failures the current corruption tests capture and which they leave out.

5 comments
AuthorsOpenReview ↗

Response to RNAQ (1/2): Absolute Rankings and Re-pretraining

We thank the reviewer for the constructive comments and the pointer to Ferrini et al. All four questions are addressed with new results in the revised manuscript (changes highlighted in blue).

W1/Q1: drop-based vs. absolute ranking. The main cross-axis patterns remain supported: Insights 1–2 under absolute performance, and Insight 3 under signed gaps (§3.3). Appendix F (Table 11b) re-ranks the eight methods evaluated on every axis by absolute performance and by the signed gap.

  • BACE example. We agree with the reviewer's reading: in absolute scaffold-test AUC, OFA is best on BACE (66.6 vs. 56.9 for GraphSAGE, which has the smallest gap), and BGRL/GIT on Tox21 (76.0). §3.2.2 now states that the smallest gap need not coincide with the best scaffold-test performance, and the leader still changes across datasets (Finding 2). The inductive-KG results are already reported in absolute MRR.
  • Finding 1 in absolute terms. In Table 1's absolute Sev5 accuracy, LLaGA ranks 6th of 10 under feature noise but 9th of 12 under edge deletion.
  • Model selection. Selecting by standard-split clean accuracy finds the best method under the strongest feature noise on only 8 of 19 datasets (up to 24.6 points worse) and under degree shift on only 7 of 13; for imbalance and attribution, clean-accuracy rankings show little agreement with the reliability rankings (τ = −0.01 and 0.01). These conditions therefore need direct testing (§5, Appendix F).

Average rank (1 = best) of the eight methods evaluated on every axis (Table 11b; attribution from Table 11):

MethodFeat. noise (abs.)Edge del. (abs.)Degree OOD acc.Attribution
GCN3.33.44.85.6
GAT4.84.26.26.5
GraphSAGE3.93.63.42.2
BGRL3.54.83.25.2
GraphMAE2.22.62.45.4
UniGraph25.06.27.27.0
GIT6.44.53.22.5
GFT6.96.85.61.5

W2/Q2: pretraining overlap in temporal and inductive-entity experiments. Yes. We re-pretrained BGRL, GraphMAE, GIT, UniGraph2, GFT and LLaGA after removing all arXiv papers from 2017 onward (the temporal OOD test period; 59% of arXiv nodes) and the union of the held-out test entities across the inductive splits of WN18RR and FB15K237 (about 58% of entities) together with their edges (about 18% of KG edges remain), and re-ran the original evaluation protocol (Appendix E, Table 10b).

  • Changes relative to run-to-run variability. All changes in the unfavorable direction are smaller than one combined standard deviation, and every larger change is an improvement (e.g., GFT FB15K237 Hits@10 0.364 → 0.379; LLaGA WN18RR Hits@10 0.270 → 0.325).
  • Main patterns remain consistent. Among the re-pretrained methods, GraphMAE and UniGraph2 keep the two smallest temporal gaps (13.5 and 13.1) and GIT and LLaGA the two largest (20.4 and 20.8), and the KG leader still differs between WN18RR and FB15K237; on WN18RR, BGRL and GraphMAE remain within run-to-run variation of each other (0.216 ± 0.020 vs. 0.225 ± 0.012). §3.2.2 and §4 state this result.

Before → after removing the OOD test data from pretraining (Table 10b):

MethodarXiv temporal gap ↓WN18RR MRR ↑FB15K237 MRR ↑
BGRL14.51 → 16.22.231 → .216.088 → .091
GraphMAE13.55 → 13.49.224 → .225.121 → .114
GIT20.47 → 20.37.094 → .092.161 → .164
UniGraph214.03 → 13.07.148 → .154.064 → .066
GFT18.81 → 16.26.157 → .173.174 → .181
LLaGA21.78 → 20.80.152 → .172.082 → .080
AuthorsOpenReview ↗

Response to RNAQ (2/2): GNNExplainer and Feature Missingness

Q3: a second explainer that scores edges directly. We added GNNExplainer, which learns an edge mask directly, under the same deletion protocol for all eight methods. Its method ranking moderately agrees with the gradient-saliency ranking (mean per-dataset Kendall τ = 0.59, from 0.29 on Elec-Computers to 0.93 on WikiCS), and the same three methods (GFT, GraphSAGE, GIT) form the top three by average rank under both explainers (Appendix G.5, referenced in §3.2.5).

Q4: feature missingness (Ferrini et al., ICML 2026). Following Ferrini et al., we added three test-time missingness mechanisms: element-wise MCAR, node-wise MCAR and value-dependent MNAR, at rates 0.1–0.9 with mean imputation, for the eight methods evaluated on every axis, with models trained on complete features (Appendix G.1.3, Table 11c).

  • Dense text embeddings do not mask missingness. At 90% missingness, accuracy drops on average over four datasets by 28–40 points under both MCAR mechanisms and by 8–18 points under MNAR.
  • Gaussian noise is not a proxy for missingness at high severity. Method rankings at 90% missingness agree only weakly to moderately with rankings under the strongest feature noise (mean τ = 0.16–0.50 across mechanisms), whereas rankings at 50% missingness agree more with those at the middle noise level (τ = 0.63–0.69). This extends Finding 1 (robustness is signal-specific).
  • §3.2.1 points to these results. With these additions, the corruption tests cover deployment-time feature noise, edge loss and feature missingness, and leave out training-time missingness and missingness-aware models (§4).

Accuracy (%) at 90% test-time missingness, averaged over CiteSeer, DBLP, PubMed and WikiCS (Table 11c):

MethodElement MCARNode MCARMNAR
GCN39.337.364.5
GAT42.839.564.7
GraphSAGE45.237.266.0
BGRL33.933.454.8
GraphMAE38.638.859.8
UniGraph234.542.356.5
GFT37.536.154.0
GIT39.334.760.1

Thank you for the detailed response and the substantial additional experiments. The absolute-performance and signed-gap analyses (Table 11b), the re-pretraining study (Table 10b), the GNNExplainer comparison, and the missingness experiments address my main concerns, and I have verified that the corresponding changes are in the revised manuscript. I am raising my score accordingly.

A few minor points remain:

  • OFA, which also pretrains on the shared corpus and is the leader on the arXiv temporal split and on FB15K237, is not included in the re-pretraining study. Please include it or explain why it was excluded.
  • Finding 1 is still supported only by drops in the main text. A brief absolute-performance check (e.g., rank agreement between the two corruption channels in absolute terms) would make it consistent with the rest of the revision.
  • The GNNExplainer results are reported only in the text; a per-method table in Appendix G.5 would be helpful.
Reviewer_UXR2OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces GRL-Reliability, a benchmark for graph representation learning covering corruption robustness, distribution shift, class imbalance, fairness, and attribution fidelity. It compares twelve methods from four families over twenty-five datasets, although coverage varies by evaluation axis. The framework standardizes text features and the graph pretraining corpus where applicable, while keeping method-specific adaptation procedures. The results show condition-dependent rankings and trade-offs across reliability dimensions. The appendices add extended evaluations, analyses on pretraining-unseen datasets, and statistical comparisons.

Critical strengths
  1. The benchmark provides a useful common framework for multiple reliability dimensions. It compares several method families under a range of conditions and goes beyond clean-task performance. The corruption-severity and imbalance-ratio sweeps are useful for seeing where performance deteriorates and for choosing methods under specific conditions.
  2. The supporting analysis improves the credibility of the evaluation. The authors disclose pretraining overlap and provide analyses on pretraining-unseen datasets. The appendices also include statistical tests and rank-agreement analyses, and the authors acknowledge where the evidence does not support fine-grained rankings. This makes the benchmark more informative and easier to assess.
Critical weaknesses
  1. Gap-based rankings do not consistently reflect useful OOD performance. In Table 2, UniGraph2 has the smallest scaffold gap on Tox21, 5.4, but its scaffold AUC of 70.2 is the lowest among the listed methods. The absolute-gap criterion in Table 12 also penalizes improvements: GIT improves from 40.14 to 45.24 on AmazonRatings but gets a larger absolute gap than GCN. The underlying performances are reported, but the paper does not sufficiently separate stability of performance from predictive utility under the shifted distribution. This affects the OOD rankings and the model-selection conclusions drawn from them.
  2. The clipped attribution score is not sufficiently validated. In Table 17, BGRL on Tolokers has a negative mean raw saliency Fid+ of −4.1 but a positive characterization-score lift of +8.2. This can follow from the stated per-node clipping procedure, but it also shows that positive lift does not necessarily mean salient-edge removal reduces prediction confidence on average. The paper needs to establish what this score actually supports about attribution quality, and whether the main rankings remain stable under an analysis of signed raw confidence changes.
Questions for authors
  1. Using the existing results, how do the central OOD rankings and cross-axis conclusions change when assessed with both OOD performance and signed ID-to-OOD degradation? In particular, how should the Tox21 and AmazonRatings examples above inform model selection?
  2. Can you compare saliency and random ablation using paired raw confidence changes before clipping, including the fraction of examples where salient-edge removal decreases confidence? Do the main attribution conclusions still hold under that analysis?
3 comments
AuthorsOpenReview ↗

Response to UXR2: Absolute Rankings and Unclipped Attribution

We thank the reviewer for the precise and constructive comments. Both main concerns are addressed in the revised manuscript (changes highlighted in blue).

W1/Q1: gap-based OOD ranking vs. usefulness under shift. We agree that a small gap does not by itself indicate better performance under shift. The revised manuscript separates the two:

  • The main cross-axis patterns remain supported: Insights 1–2 under absolute performance, and Insight 3 under signed gaps (§3.3). Appendix F (Table 11b) re-ranks the eight methods evaluated on every axis by absolute performance and by the signed gap. GFT leads attribution but ranks last under both corruptions in absolute terms, while GraphMAE ranks first under both; absolute edge-deletion accuracy and attribution remain unrelated (τ = −0.03). The signed degree-gap ranking closely follows the original gap ranking (τ = 0.85), although its leader differs from that under absolute degree-OOD accuracy (BGRL vs. GraphMAE).
  • Finding 2 holds in absolute terms. In absolute scaffold-test AUC, OFA is best on BACE (66.6) and BGRL/GIT on Tox21 (76.0), so the leader still changes across datasets (§3.2.2). The inductive-KG results are already reported in absolute MRR.
  • Model selection. Selecting by standard-split clean accuracy finds the best method under the strongest feature noise on only 8 of 19 datasets (up to 24.6 points worse) and under degree shift on only 7 of 13 (Appendix F). Reliability under these conditions therefore needs direct testing, which the benchmark provides.

Average rank (1 = best) of the eight methods evaluated on every axis (Table 11b; attribution from Table 11):

MethodFeat. noise (abs.)Edge del. (abs.)Degree OOD acc.Degree signed gapAttribution
GCN3.33.44.84.45.6
GAT4.84.26.26.26.5
GraphSAGE3.93.63.44.42.2
BGRL3.54.83.23.25.2
GraphMAE2.22.62.43.35.4
UniGraph25.06.27.25.77.0
GIT6.44.53.24.02.5
GFT6.96.85.65.01.5

The two examples.

  • Tox21: the scaffold-test AUC should drive selection, i.e. BGRL or GIT (76.0) rather than UniGraph2 (70.2), whose small gap comes with the lowest AUC. §3.2.2 now states that the smallest gap need not coincide with the best scaffold-test performance, the Table 2 caption clarifies that bold on Δ marks the smallest gap, and App. D.2 notes that ΔAUC must be read together with the scaffold-test AUC.
  • AmazonRatings: Table 12 no longer uses the |Gap| criterion; its caption states that negative gaps mean OOD accuracy exceeds ID accuracy and that Gap should be read together with OOD accuracy. GIT has both the lowest signed gap (−5.10) and the highest OOD accuracy (45.24), so both criteria select it.

W2/Q2: what the clipped attribution score supports. We agree that a positive clipped lift alone does not show that removing salient edges lowers confidence on average. We therefore report, in a separate paired evaluation, per-node comparisons of salient vs. random edges on the same nodes and edge budget, without clipping (Appendix G.5, Table 17b):

  • Signed ΔFid+. Saliency produces a significantly larger confidence drop than random ablation in 56 of 64 method–dataset cells (paired sign-flip permutation test, p < 0.05). BGRL/Tolokers, the cell the reviewer identified, is the only significantly negative one. In this paired evaluation, its saliency-minus-random ΔFid+ is −5.2 points (a different quantity from the saliency-only Fid+ of −4.1 in Table 17, with the same sign), and confidence decreases for 21% of nodes under saliency vs. 55% under random ablation.
  • Fraction of nodes whose confidence decreases. 69% under saliency vs. 53% under random ablation on average, and higher for saliency in 58 of 64 cells.
  • Ranking stability. The method ranking under the clipped lift agrees with the ranking under signed ΔFid+ (mean Kendall τ = 0.84) and under an absolute-value fidelity variant (τ = 0.88); GFT ranks first under all three, with GraphSAGE and GIT in the next two positions.

Signed, unclipped comparison summarized per method (Table 17b):

MethodDatasets where saliency is significantly better than randomNodes with decreased confidence, saliency / random (%)Signed rank
GCN7/862.7 / 50.26.1
GAT6/857.9 / 50.56.4
GraphSAGE8/884.7 / 56.62.4
BGRL7/857.5 / 49.76.1
GraphMAE8/865.0 / 52.35.4
UniGraph24/855.1 / 50.56.0
GFT8/885.2 / 55.11.1
GIT8/885.6 / 55.42.5

The clipped lift therefore supports the method-level comparison, while individual cells can differ, as for BGRL/Tolokers. §3.2.5 now states this explicitly, and App. D.5 describes the signed and absolute-value variants.

The authors have addressed all my concerns. I have increased the score to “3. Weak acceptance”. However, it would be better to check the Protein-HS and ML1M-cls in Appendix G.1, Fig. 6-7, which did not appear in Appendix A, Table 4.

We sincerely thank the reviewer for the constructive feedback throughout the discussion and for increasing the score. We will add Protein-HS and ML1M-cls to Table 4 in the final version.

Reviewer_75nPOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

Three main contributions are: Our contributions are:

  1. Benchmark scope. GRL-Reliability positions reliability evaluation at the level of GRL, covering topology-only graph embeddings, supervised GNNs, self-supervised GRL methods, and GFMs across diverse graph tasks and domains.
  2. Multi-axis reliability protocol and evaluation. GRL-Reliability evaluates five deployment relevant evaluation axes: corruption robustness, OOD generalization, class imbalance, fairness, and interpretation. It reports per-axis and subcondition results rather than collapsing graph reliability into a single aggregate score.
  3. Cross-axis empirical insights. GRL-Reliability shows that even structurally related testscan expose distinct reliability properties, that foundation-era methods exhibit axis-specific rather than broad reliability advantages, and that degree shift and rare-class coverage remain challenging across the evaluated method set. These patterns remain qualitatively consistent on pretraining-unseen evaluation graphs.
Critical strengths
  1. Benchmark scope. GRL-Reliability positions reliability evaluation at the level of GRL, covering topology-only graph embeddings, supervised GNNs, self-supervised GRL methods, and GFMs across diverse graph tasks and domains.
  2. Multi-axis reliability protocol and evaluation. GRL-Reliability evaluates five deployment relevant evaluation axes: corruption robustness, OOD generalization, class imbalance, fairness, and interpretation. It reports per-axis and subcondition results rather than collapsing graph reliability into a single aggregate score.
  3. Demographic fairness is currently evaluated on only one compatible dataset, limiting the generality of conclusions on this axis. Finally, the pretraining-unseen analysis removes direct evaluation-graph overlap but does not fully isolate the effects of pretraining composition.
Critical weaknesses
  1. The current benchmark focuses on five evaluation axes, leaving concerns such as calibration, adaptive adversarial robustness, and privacy outside its scope. 2.Method coverage is also necessarily selective and does not include all architecture families or backbones, so the empirical findings should be interpreted with respect to the evaluated method set.
Questions for authors

Please address the following:

  1. The calibration, adaptive adversarial robustness, and privacy issues. 2.The selective method should include all architecture families or backbones, so the empirical findings should be interpreted with respect to the evaluated method set.
  2. Demographic fairness is currently evaluated on only one compatible dataset, limiting the generality of conclusions on this axis.
  3. Finally, the pretraining-unseen analysis removes direct evaluation-graph overlap. It should fully isolate the effects of pretraining composition.
  4. Some references have missing details that should be updated.
3 comments
AuthorsOpenReview ↗

Response to 75nP: Scope, Fairness, Pretraining, and References

We thank the reviewer for the positive assessment and the helpful suggestions.

Scope (calibration, adaptive attacks, privacy) and method coverage. Thank you for raising these; we agree they are valuable directions. As noted in our Limitations (§4), we selected these five axes to cover complementary deployment risks (input corruption, distribution shift, label imbalance, group disparity and attribution fidelity) while keeping evaluation protocols comparable across compatible methods. The twelve evaluated methods span four families, and we interpret the findings with respect to this method set. Each suggested risk would need its own protocol (a common threat model for adaptive attacks, comparable membership definitions for privacy, and aligned probabilities across output heads for calibration), which we see as promising future work beyond the scope of this paper.

Fairness on one dataset. We agree that a single dataset limits the generality of demographic fairness findings. As noted in §3.2.4, Tolokers is the only dataset in our collection that exposes a compatible sensitive attribute. We therefore present demographic fairness as an exploratory case study rather than drawing cross-dataset conclusions. The fairness component of our cross-axis analysis instead uses structural (head–tail degree) fairness, which covers eight datasets. Extending demographic fairness evaluation to additional datasets with compatible sensitive attributes remains future work.

Pretraining composition. To address this point, we re-pretrained BGRL, GraphMAE, GIT, UniGraph2, GFT and LLaGA with all temporal OOD test nodes and inductive test entities removed. This removes 59% of arXiv nodes and 82% of KG edges from pretraining, so the composition changes substantially, and the temporal and inductive-entity results of these methods remain qualitatively consistent (Appendix E, Table 10b; details in our response to RNAQ). This is a sensitivity check rather than a full isolation of composition effects, which §4 continues to note.

References. We have completed the incomplete bibliographic entries:

  • "Text-space Graph Foundation Models: Comprehensive Benchmarks and New Insights": arXiv preprint → published version (NeurIPS 2024, Datasets and Benchmarks Track, pp. 7464–7492).
  • "DecodingTrust: A Comprehensive Assessment of Trustworthiness in GPT Models": first 10 authors + "et al." → full list of 19 authors.
  • "A Deep Learning Approach to Antibiotic Discovery" (Cell, 2020): first 10 authors + "et al." → full list of 20 authors.
  • "TAGLAS: An Atlas of Text-Attributed Graph Datasets in the Era of Large Graph and Language Models": incomplete preprint entry → standard arXiv citation (arXiv:2406.14683).
  • New references for the added experiments: "Rethinking GNNs and Missing Features: Challenges, Evaluation and a Robust Solution" (ICML 2026) and "GNNExplainer: Generating Explanations for Graph Neural Networks" (NeurIPS 2019).

I am satisfied with all authors' response on my suggestions. My assessment score remains no change as "3" weak accept.

We sincerely thank the reviewer for the positive assessment and constructive feedback throughout the discussion. We are glad that our responses have addressed the reviewer's suggestions.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Summary of Revisions and New Experiments

Dear Reviewers and Area Chair,

We thank all reviewers for their thoughtful and constructive feedback. We have updated the submission with a revised manuscript, in which the changes are highlighted in blue. We summarize the main changes below; detailed responses are provided under each review.

  1. Absolute performance alongside drops (UXR2, RNAQ). Appendix F adds absolute-performance and signed-gap rankings (Table 11b) and a model-selection analysis. Insights 1–2 hold under absolute performance and Insight 3 under signed gaps. Table 12 no longer ranks by |Gap|, and §3.2.2 reports the absolute scaffold-test leaders.
  2. Signed, unclipped attribution fidelity (UXR2). Appendix G.5 and Table 17b report paired saliency-vs-random comparisons without clipping: saliency is significantly better in 56 of 64 method–dataset cells, and the method ranking is stable (Kendall τ = 0.84).
  3. Pretraining overlap (RNAQ, 75nP). We re-pretrained BGRL, GraphMAE, GIT, UniGraph2, GFT and LLaGA with all temporal OOD test nodes and inductive test entities removed (Appendix E, Table 10b). Among these methods, the two smallest-gap and two largest-gap temporal methods remain the same, and the KG leader still differs across datasets.
  4. A second explainer (RNAQ). GNNExplainer recovers the same top three methods by average rank (Appendix G.5).
  5. Feature missingness (RNAQ). We added three test-time missingness mechanisms following Ferrini et al. (ICML 2026) (Appendix G.1.3, Table 11c). At 90% missingness, accuracy drops by 28–40 points under MCAR, and at high missing rates method rankings differ from those under Gaussian noise.
  6. Scope and references (75nP). §4 states the coverage of the new tests, and the incomplete bibliographic entries are completed.

Best regards,

The Authors

Dear Reviewers,

Now that the authors have responded, please review what they have said and give consideration to whether they have adequately addressed your concerns.

-The AC

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

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