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Under review as a conference paper at ICLR 2027

The Universal Classifier for Graph Learning

Abstract

While foundation models have revolutionized natural language processing and computer vision by leveraging universal vocabularies, Graph Machine Learning (GML) remains fractured due to the absence of a unified feature and structural representation across diverse domains. Existing works claiming to be Graph Foundation Models (GFMs) are typically restricted to node-level predictions or require fixed feature dimensions, failing to provide a truly task-agnostic backbone for the full spectrum of graph learning applications. In this paper, we introduce the UC, which supports arbitrary feature and class cardinalities, unifying node-, edge-, and graph-level objectives under a single similarity-based classification objective. The UC reformulates all node-, edge-, and graph-level prediction tasks as maximizing similarity in the latent space: by lifting heterogeneous features and labels into 3D latent tensors, the model learns transferable features independent of specific input schemas. This architecture allows a single pre-trained model to generalize to node classification, node regression, and link prediction across unseen graphs with varying feature semantics. Experiments show strong zero-shot transfer performance across node-, link-, and graph-level tasks.

Primary area:
foundation or frontier models, including LLMs
Keywords:
foundation model, graph foundation models, multi-task learning, in-context learning

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_uoprOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

The paper proposes the Universal Classifier (UC), a pretrained graph model that handles graphs with any number of features and classes. Every task is treated as a comparison between labeled items, called anchors, and unlabeled items, called queries. Each feature and each label entry is mapped to a DD-dimensional vector, so a node becomes an (F+C)×D(F + C) \times D matrix, where FF is the number of node features and CC is the number of classes. A GNN encoder and a transformer process these matrices, a similarity score is computed for each query-anchor pair, and the scores are averaged per class to obtain class logits. Regression is turned into classification over soft bins, link prediction compares a source node with its neighbors and with random nodes, and graph-level tasks use mean-pooled graph representations. One checkpoint, pretrained on an undisclosed mixture of node- and edge-level datasets, is evaluated without training on the target graph (called "zero-shot") and after fine-tuning. The evaluation covers node classification, node regression, link prediction, and graph regression, though the latter only in a single domain (electronic circuits). The paper reports that zero-shot UC often outperforms supervised GNNs trained on the target graph.

Critical strengths

The query-anchor formulation is simple and general. It handles arbitrary feature and class counts, and it covers node, link, and graph tasks with one similarity-based objective. The evaluation uses recent and diverse datasets.

Critical weaknesses

1. The results cannot be verified.

  • The authors release neither the code, the pretraining data, nor the parameter count (lines 305-307 and 500-505). As a result, the key condition that "no evaluation dataset appears in the pre-training mixture" (lines 308-309) cannot be checked. The statement that other pretraining mixtures give similar results (lines 501-505) comes without any evidence.
  • Withholding the parameter count is also hard to understand, since Appendix F describes a very small model: hidden size 16 in the GNN encoder and 32 in the transformer.
  • No result for UC comes with a standard deviation. The paper explains that retraining the model is "prohibitively expensive" (lines 312-313), but Table 1 reports five ablated variants, and each of them is a model retrained from scratch (lines 423-424). For fine-tuning, the paper only states that seed randomness "stays below 0.1% in most cases" (line 314).
  • Table 1 calls a 2-layer transformer "detrimental" (lines 427-428), while Appendix F states that the model has 2 transformer layers (line 915), so it is unclear which configuration produced the reported results.
  • The description of the transformer misrepresents the cited models. The paper states that only queries are updated by cross-entity attention, "as is standard in tabular foundation models" (lines 209-211), and that this "follows the same convention" as TabPFN and TabICL (lines 811-814). However, in these models the labeled rows attend to each other, and only their attention to the unlabeled rows is removed. In Algorithm 1 (steps 13-18), each anchor attends only to its own features and labels, so it never sees the other anchors. Either the description is wrong, or the model differs from the cited ones in a way the paper does not discuss.

2. The baselines are weaker than published results, and several claims do not match the tables.

  • In Table 4, the supervised GNN results (43.93% accuracy on roman-empire, 47.18% on amazon-ratings) are the GAT results from the appendix of the GraphAny paper, which uses the same split and metric as the paper that introduced these datasets. In the same GraphAny table, even an MLP reaches 65.80% on roman-empire, and the dataset paper reports up to 88.75% (GAT-sep) and 53.63% (GraphSAGE). Against these results, zero-shot UC (78.61% and 52.83%) is worse than the best GNNs, so the claim that UC "in most cases" surpasses supervised GNNs (lines 366-367) is not supported.
  • For node regression, the paper claims that UC is "matching or exceeding the transfer performance of specialized tabular foundation models" (line 377). The only foundation model in this comparison is GraphPFN (Figure 4, Table 6). However, in all three cases where GraphPFN is reported, zero-shot UC is worse: 60.54 vs 63.55 on city-roads-M, 66.09 vs 73.27 on twitch-views, and 50.85 vs 61.77 on artnet-views. Even the fine-tuned UC stays below zero-shot GraphPFN.
  • For graph regression, zero-shot UC has a relative squared error above 1.0 on three of six targets in Table 8, which, by the paper's own definition (line 386), is worse than always predicting the training mean. Nevertheless, the abstract claims "strong zero-shot transfer performance across node-, link-, and graph-level tasks". Also, graph classification is described in Figure 1 and Section 2.5 but never evaluated.

3. The zero-shot results are hard to believe without the evaluation code.

On the RL split of GraphLand, zero-shot UC is far above the best published results. For example, in the latest version of the GraphPFN paper, fine-tuned GraphPFN outperforms all compared methods, including GNNs and gradient boosting, on every GraphLand dataset evaluated there with the RL split. Yet zero-shot UC reaches 65.46 vs 53.49 average precision on artnet-exp, 86.53 vs 80.90 on city-reviews, and 67.18 vs 62.80 on tolokers-2. Gains of this size from a small model that never saw these graphs need an explanation.

Until the authors release the code that applies the model to the evaluation datasets, I find it hard to trust these results.

Questions for authors
  1. I understand that organizational policy limits what can be released. Could you release only the evaluation code, without the weights and the pretraining code? This would allow checking how the model is applied to the evaluation datasets.
  2. Why are the supervised GNN results in Table 4 taken from the GraphAny paper, although the dataset paper reports much higher results under the same split?
  3. Do anchors attend to other anchors in cross-entity attention? If not, how does the model compare with a variant where they do, as in TabPFN and TabICL?
  4. How many anchors are used at test time on each dataset, and how are they chosen when the training split is larger than the anchor budget?
13 comments

We thank the reviewer for the constructive comments and would like to address the raised concerns:

(W1,Q1) release neither the code, the pretraining data, nor the parameter count… (W1) No result for UC comes with a standard deviation (W3) Until the authors release the code that applies the model to the evaluation datasets, I find it hard to trust these results

Please find a discussion on data mixtures, parameter count and training flops in R5 of the General Response.

We understand why withholding code limits verification, and would like to point out that under ICLR 2027 Author Guidelines, code submission is encouraged rather than mandatory, and the ICLR Code of Ethics obligates authors to honor intellectual-property and confidentiality agreements alongside transparent paper and appendix documentation.

Still, we do not ask you to accept surprising results on faith. In the General Response to your critique, we added checkpoints trained with more random seeds, commented on graph regression performance, expanded evaluation to 7 new graph-level tasks, fixed baseline and manuscript discrepancy, and verified via label permutation that predictions depend causally on anchor labels.

(W1) Table 1 calls a 2-layer transformer "detrimental"…while Appendix F states that the model has 2 transformer layers

Thank you for catching this. It’s a typo and we ablated a 1-layer transformer encoder there, will be fixed.

(W1,Q3) only queries are updated by cross-entity attention, “as is standard in tabular foundation models"…Algorithm 1 (steps 13-18)…Do anchors attend to other anchors…? Either the description is wrong, or the model differs from the cited ones in a way the paper does not discuss

Thank you for catching this, the description is wrong. In UC, anchors attend to other anchors - the intra-entity block in Figure 2 does include anchor-to-anchor attention, we will correct Section 2.3, Figure 2, and Algorithm 1.

We also tested removing anchor-to-anchor attention in R5 of the General Response: it improves classification and regression yet hurts link prediction and circuit RSE , so we retain it for balanced multi-task stability.

(W3) RL split of GraphLand, zero-shot UC is far above the best published results…Gains of this size…need an explanation

We hypothesize the reason could be in a different ICL mechanism - tabular models pool rows to a fixed number of latents while UC is able to process each data point independently (and at scale). To test whether gains reflect genuine in-context graph inference rather than feature memorization, we ran inference interventions isolating the GNN propagation and test-time anchor labels in R5 of the General Response and find

(Q4) How many anchors are used at test time on each dataset, and how are they chosen when the training split is larger than the anchor budget?

By default we use all anchors, and UC can process arbitrarily large labeled datasets in contrast to GraphPFN. If it happens that the training split is larger than the anchor batch size, we randomly chunk the anchors and score the batches sequentially. We found a sufficiently large anchor batch size (1024+) reduces the sampling noise in anchor-to-anchor attention. Besides that, Figure 6 in the manuscript shows that it is possible to randomly subsample 1 to 5% of anchors and retain 80+% of the full performance.


We hope our responses address your concerns and appreciate your reconsideration of the evaluation and increasing the score.

Dear Reviewer, as the discussion period is closing soon, we would highly appreciate your response so we have a chance to address any remaining issues. We look forward to hearing from you. Thank you!

Thank you for the detailed replies and additional experiments.

  • W1 is mostly addressed.
  • Q2, Q3 and Q4 are addressed.
  • W2 is partly addressed. Zero-shot UC still loses to several supervised GNNs, so please adjust the claims about outperforming them.
  • W3 and Q1 remain unresolved. The evaluation code has not been provided, and I explain my specific concern below.

1. What changed when you "improved the model"?

In R1, you write "improved the model" and report two additional training seeds and averaging predictions over ten forward passes. The zero-shot regression results on the RL split improved substantially: R2R^2 increased from 60.54 to 64.91 on city-roads-M, from 66.09 to 75.42 on twitch-views, and from 50.85 to 62.08 on artnet-views. What exactly changed in the architecture, training, or evaluation? How much of this improvement comes from averaging predictions, and how much from the model changes? Did the ablations in R5 use the improved model?

2. I am concerned that labels of validation or test nodes may reach the model through neighboring nodes.

After seeing these strong results, thinking about how they could have been achieved, and reading the descriptions and Algorithm 1, I am concerned that some labels may not be masked correctly. This concern motivated my request for evaluation code.

Section 2.3 describes GNN message passing over the union of sampled neighborhoods of anchors and queries, using both feature and label representations. These neighborhoods can include validation or test nodes that are neither anchors nor current queries. Algorithm 1, step 3, specifies true labels for anchors and zeros for queries, but does not specify labels for these additional nodes. Steps 7–9 then lift and propagate labels. If validation and test neighbors keep their true labels, those labels could reach queries through message passing even when the current queries' own labels are masked.

You say that neighboring labels are "known from the training set." Could you therefore confirm that, in the evaluation used for your main results, all validation and test labels are masked before they are encoded and passed through the GNN, including labels of neighboring nodes that are neither queries nor anchors in the current batch? Please explain how the code ensures this. If only training labels are available throughout the sampled graph, the leakage described above cannot occur.

3. Which results can the community reproduce?

While I admit that the code release is not mandatory, I also note that the ICLR Code of Ethics says:

Methods and results should be presented in a way that is transparent and reproducible.

I believe that the model itself could be implemented from the paper once the descriptions above are corrected. However, the paper does not identify the pretraining datasets, so the community cannot repeat pretraining and reproduce the evaluation results from scratch.

An actionable step would be to pretrain UC on a publicly available collection of datasets, a synthetic prior, or a combination of the two, and report the evaluation results. If UC achieves strong performance in this setting too, this will make the paper more reproducible and verifiable.

Reviewer_5UEqOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes Universal Classifier (UC), a schema-invariant graph learning framework that unifies node-, edge-, and graph-level tasks through query-anchor similarity. UC combines a GNN encoder with a query-anchor Transformer to learn representations across different feature and label spaces, and makes predictions by aggregating similarity scores without task-specific prediction heads. Experiments evaluate its zero-shot generalization to unseen graphs across node classification, node regression, link prediction, and graph regression, along with additional fine-tuning results.

Critical strengths

S1. Unified graph learning across multiple task levels.

The paper presents a single schema-invariant model capable of handling node-, edge-, and graph-level tasks without task-specific prediction heads. Combining these different task levels within a single pretrained model is a meaningful step toward general-purpose graph foundation models.

Critical weaknesses

W1. Limited novelty of similarity-based task unification and missing discussion of related work.

UC's core query-anchor prediction mechanism closely resembles EquiTabPFN [1], which already employs similarity-weighted aggregation of training labels through a non-parametric decoder. UC's class-wise similarity aggregation follows a similar principle, with additional normalization by class support size. Moreover, its extensions to different graph tasks largely rely on established techniques, including pairwise similarity for link prediction, graph pooling, and regression discretization.

Despite these similarities, EquiTabPFN is neither cited nor discussed in the paper. The authors should clarify the methodological novelty of the proposed task unification beyond existing similarity-based approaches and explicitly discuss its relationship to EquiTabPFN.

W2. Insufficient empirical evidence for universal zero-shot generalization.

Despite emphasizing universal zero-shot generalization across graph tasks, the experimental results provide limited support for this claim. In graph regression, zero-shot UC performs worse than the training-mean baseline on three of six targets. Moreover, UC underperforms GraphPFN on all three directly comparable node regression settings. The link prediction evaluation is also limited to 250 test edges per dataset with 200 randomly sampled candidates, raising concerns about the robustness of the reported results. These limitations weaken the empirical evidence for the claimed universal generalization capabilities.

W3. Insufficient experimental validation and reproducibility.

The experiments do not sufficiently establish the benefits of the proposed unified framework. The ablation study is restricted to two node-level datasets, without examining the contributions of individual components to link- and graph-level tasks or the benefits of joint task pre-training. Furthermore, the pre-training data mixture, training code, and parameter count are not disclosed, and results are reported from a single checkpoint without uncertainty estimates. These limitations make it difficult to isolate the contributions of the proposed framework and independently verify the reported results.

[1] Arbel et al., EquiTabPFN: A Target-Permutation Equivariant Prior Fitted Networks, NeurIPS 2025

Questions for authors

Q1. How does UC's similarity-based prediction mechanism fundamentally differ from EquiTabPFN, and what is the key methodological novelty of the proposed task unification?

Q2. Could the authors evaluate link prediction with larger test sets and more challenging negative samples?

Q3. Could the authors provide ablations on link- and graph-level tasks and compare joint versus task-specific pre-training to validate the benefits of task unification?

Q4. Could the authors provide more details on the pre-training setup and uncertainty estimates to improve reproducibility and reliability?

3 comments

We thank the reviewer for the constructive comments and would like to address the raised concerns:

(W1, Q1) Limited novelty, missing discussion of EquiTabPFN

Thank you for pointing this out. EquiTabPFN does share some similarities with UC and we will add them to our related works discussion. The key methodological novelties in UC compared to EquiTabPFN are:

  • Multi-task: EquiTabPFN covers classification only; UC covers regression, link prediction, graph regression and graph classification.

  • Graph Topology: UC is able to leverage connectivity structure among nodes while EquiTabPFN assumes i.i.d. tabular rows; ablating UC's GNN component significantly drops the performance (R5 in General Response).

  • Avoids sample-prior bias: EquiTabPFN sums softmax weights over training anchors before its MLP (Section 4.3), baking class counts ∣Ac∣\lvert A_c\rvert into predictions; UC subtracts log⁡∣Ac∣\log\lvert A_c\rvert (Section 2.3) without a post-kernel MLP, avoiding class-count skew.

  • Employs feature/label attention mechanisms: EquiTabPFN embeds covariates into 1 token (U∈Rd×pU \in \mathbb{R}^{d \times p}, max p=100p=100; Sections 4.1–4.2, Appendix B) without target-to-target or per-feature attention.

(W2, Q2) Insufficient empirical evidence for universal zero-shot generalization

Please have a look at the General Response where we addressed the concerns about baselines, ran comparisons with GraphPFN, added more graph-level tasks, commented on graph regression performance, added more checkpoints to compute stds, and ran more link prediction evals. We are happy to elaborate further if you have any remaining questions.

(W3, Q3, Q4) Insufficient experimental validation and reproducibility

Please have a look at R5 in the General Response where we elaborated on the mixture, training flops, and added more data and model ablations. Please let us know if you have any further questions.


We hope our responses address your concerns. We would greatly appreciate your reconsideration of the evaluation and increasing your score.

Dear Reviewer, as the discussion period is closing soon, we would highly appreciate your response so we have a chance to address any remaining issues. We look forward to hearing from you. Thank you!

Dear Reviewer 5UEq, as today is the last day of the discussion period, we wanted to follow up one more time in case you have any remaining questions or concerns we can address. Thank you!

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

This paper proposes the Universal Classifier (UC), a graph foundation model that handles node-, edge-, and graph-level tasks across arbitrary feature and label spaces. They argue that existing GFMs either are limited to a single task or require fixed feature dimensions. Their method proposes to lift each feature and label scalar into a shared latent space, then frame every task as in-context similarity between unlabeled queries and labeled anchors, with scores pooled by class. This results in a single pretrained model trained with one cross-entropy objective and no task-specific heads. They validate it on node classification, node regression, link prediction, and graph regression benchmarks in zero-shot and fine-tuned settings, along with an inference-time scaling analysis. Results show strong zero-shot node classification relative to schema-invariant baselines, competitive link prediction against supervised models, and graph-level transfer that is largely realized after fine-tuning.

Critical strengths

(S1) The paper clearly identifies a gap in many existing GFMs, where existing approaches either only deal with one task or a fixed feature space. It addresses this directly by framing every task as similarity to labeled anchors, enabling a single in-context model across task levels and arbitrary feature and label spaces.

(S2) Zero-shot node classification is strong with large gains over other schema-invariant models in the relevant settings.

Critical weaknesses

(W1) The empirical evaluation raises some concerns. In particular, the supervised GNN baseline on Roman-empire achieves only ~40% accuracy, substantially below the numbers reported in prior work (Platonov et al., 2023), raising questions about baseline tuning. For node regression, GraphPFN outperforms UC in every setting where both results exist, despite the paper's claim of matching or exceeding tabular foundation models. Also, the evidence for graph-level generalization is limited to regression on a single domain, with no graph classification experiments and poor zero-shot performance on several targets. While the results generally remain strong across other settings, these results weaken the empirical support for the paper's broader claims. I’d like to see more commentary on these, confirmation that baselines are properly tuned, and more careful qualification of the results in the text.

(W2) The paper claims to be the first model to handle node-, edge-, and graph-level tasks without task-specific heads or fixed feature and class dimensions, but doesn’t discuss Prodigy (Huang et al., 2023) or OFA (Liu et al., 2024), which both frame graph tasks as comparing a query to labeled examples, with OFA covering all three task levels without heads. UC’s distinction appears to be schema invariance over raw features, and I’d like to see discussion in the paper to position the work explicitly against these prior works.

Questions for authors

(Q1) The authors state that organizational policy prevents disclosing the pretraining mixture and parameter count, and that repeated pretraining is prohibitively expensive. Can they at least provide aggregate statistics about the corpus (domains, task composition, synthetic proportion), an approximate model size, and quantitative evidence supporting the claim that different pretraining mixtures yield similar performance?

(Q2) The computational cost of UC scales with F+CF+C, including a quadratic term from intra-entity attention, and some datasets have very large feature counts (e.g., full-cora with 8,710). What are the memory and runtime on these datasets compared to the baselines? Reporting runtime only for roman-empire, amazon-ratings, and arxiv leaves this unclear.

6 comments

We thank the reviewer for the constructive comments and would like to address the raised concerns:

(W1) The empirical evaluation raises some concerns

Please have a look at the General Response where we addressed the concerns about baselines, ran comparisons with GraphPFN, added more graph-level tasks, commented on graph regression performance, and added stds. We are happy to elaborate further if you have any remaining questions.

(W2) No discussion of Prodigy and OFA

Thank you for flagging this missing comparison. We will remove "first" and add structured comparisons to Prodigy and OFA.

GraphAny and GraphPFN accept arbitrary raw numeric feature widths but address node tasks alone, limiting cross-regime transfer that is expected of a GFM. Prodigy and OFA do not satisfy the GFM definition along the orthogonal axis: both unify multiple task levels via in-context prompt nodes, yet require graphs mapped into fixed 768-dim language-model embeddings (domain-matched spaces in Prodigy; text-attributed inputs and class text zero-shot in OFA, which leaves regression to future work).

Neither applies out of the box with arbitrary raw numeric features without building a text pipeline. UC accepts arbitrary raw (F,C)(F, C) inputs across node classification, node regression, link prediction, and graph tasks.

(Q1) Aggregate statistics about the corpus, an approximate model size, and quantitative evidence supporting the claim that different pretraining mixtures yield similar performance?

Please have a look at R5 in the General Response where we elaborated on the mixture, training flops, and added more ablations. Please let us know if you have any further questions.

(Q2) The computational cost of UC scales with F+CF+C, e.g., full-cora with 8,710 features. What are the memory and runtime on these datasets compared to the baselines?

We use efficient message passing and attention TPU kernels when processing datasets with many features and never materialize full tensors in HBM. Memory consumption never exceeds 10 GB HBM and allows to run inference on those datasets in minutes.


We hope our responses address your concerns. We will include all suggested clarifications and additional experimental results in the revised submission with the appropriate discussion. We would greatly appreciate your reconsideration of the evaluation and increasing your score.

Dear Reviewer, as the discussion period is closing soon, we would highly appreciate your response so we have a chance to address any remaining issues. We look forward to hearing from you. Thank you!

Thank you for the detailed responses. I appreciate the authors’ efforts, which have strengthened the paper. I have a few remaining questions:

Empirical evaluation (W1): The updated GraphPFN comparisons mostly address my concern, and the additional graph-level benchmarks provide stronger evidence for UC’s generality. I encourage the authors to emphasize UC’s broad zero-shot applicability, and briefly discuss the observed variation in graph-level performance and potential failure modes.

One minor question: what is varied across UC’s 10 ensemble forward passes? Given its permutation-invariant architecture, things like column permutation used in the PFN works wouldn’t apply?

Comparison to existing baselines (W2): I consider this concern addressed. I encourage the authors to lean in on the framing of task universality and schema invariance, while appropriately acknowledging related work.

Pretraining and ablations (Q1): The additional experiments largely address my concerns and reveal interesting tradeoffs between specialized and joint-task pretraining. However, coarse statistics on pretraining domains, synthetic-data proportions, and model size are still missing, and I think they would improve the technical discussion in the paper.

Computational scalability (Q2): The provided explanation is reassuring, but quantitative inference times on high-dimensional datasets, ideally compared against representative baselines, would help clarify practical scalability.

Overall, I view the rebuttal positively and appreciate the substantial improvements. I am inclined to increase my overall score, pending clarification of the remaining questions above.

Comments on the paper

4 comments

We thank reviewers for their constructive feedback and would like to address here the common concerns.

(R1) GraphPFN outperforms UC (ZXUN, 5UEq), missing standard deviation (uopr)

We would like to note that reported GraphPFN numbers are ensembled from 10 forward passes while UC performance was reported without any ensembling. After improved the model and training with 2 more random seeds (3 seeds overall) to add standard deviations, we report ensembled results from 10 forward passes as well. Please find the updated tables below.

Classification:

Method (RL / RH)hm-categories (Acc)tolokers-2 (AP)city-reviews (AP)artnet-exp (AP)Average
GraphPFN (Zero-Shot)55.25±0.75 / —61.29±0.12 / —80.25±0.05 / —51.79±0.11 / —62.15 / —
UC (Zero-Shot)57.04±0.38 / 61.83±1.2766.81±1.39 / 66.03±1.7185.48±0.53 / 87.09±0.4668.25±0.11 / 67.73±0.6169.39 / 70.67
GraphPFN (FT)78.67±0.20 / —62.80±0.39 / —80.90±0.03 / —53.49±0.81 / —68.97 / —
UC (FT)61.78±0.75 / 75.68±0.2073.45±0.14 / 80.32±0.3788.50±0.18 / 89.63±0.0570.83±0.30 / 74.38±0.3673.64 / 80.00

Regression:

Method (RL / RH)city-roads-Mcity-roads-Ltwitch-viewsartnet-viewsAvg. (w/o city-roads-L)
XGBoost59.14±0.11 / 70.93±0.0553.75±0.07 / 64.62±0.0713.39±0.00 / 13.34±0.0232.74±0.04 / 36.83±0.0639.76 / 46.43
LightGBM + NFA61.18±0.03 / 72.09±0.0755.26±0.04 / 66.24±0.0860.14±0.01 / 62.14±0.0156.10±0.02 / 60.30±0.0759.14 / 64.84
GraphPFN (Zero-Shot)64.85±0.13 / —— / —73.20±0.08 / —62.79±0.08 / —66.95 / —
UC (Zero-Shot)64.91±0.08 / 78.99±0.3958.76±0.65 / 78.03±0.2575.42±0.03 / 76.48±0.0362.08±0.03 / 63.73±0.0367.47 / 73.01
GraphPFN (FT)67.30±0.21 / —— / —79.00±0.14 / —65.35±0.06 / —70.55 / —
UC (FT)65.32±0.15 / 79.60±0.2659.12±0.86 / 78.22±0.0975.46±0.01 / 76.75±0.0562.19±0.12 / 63.88±0.1267.66 / 73.41

On average, UC substantially outperforms GraphPFN on classification tasks, pars on zero-shot regression tasks, and only trails a few pp on FT regression (while having rather small std). On the other hand:

  • UC scales to dataset splits which GraphPFN cannot process (all RH splits and city-roads-L task)

  • Unlike GraphPFN with separate heads for classification and regression, UC performs all tasks with the same head, model and scoring mechanism

  • UC is able to perform link prediction and graph-level tasks out of the box, none of tabular models can do so (more on those experiments below).

(R2) Evaluating link prediction on larger pools (5UEq)

LP with 250 test edges with 200 candidates per edge (Hits@10 %↑\uparrow) with std

Methodroman-empirewiki-cscity-roads-Mtolokers-2Avg.
SEAL87.33±1.1586.53±1.9799.47±0.6179.73±0.6188.27
NBFNet88.00±0.0192.00±0.4099.20±0.0192.53±0.9292.93
BUDDY58.40±11.0983.60±4.5191.47±5.4372.93±1.2276.60
UC Zero-Shot68.67±1.2287.21±1.2898.53±0.6172.09±2.3581.63
UC Fine-Tuned83.20±1.0690.44±0.32100.00±0.0075.49±0.7787.28

On a more challenging LP setup with 1,000 test edges with 2,000 uniform candidates per edge (Hits@10 %↑\uparrow):

Methodroman-empirewiki-cscity-roads-Mtolokers-2Avg.
UC Zero-Shot49.37±4.1167.08±0.8962.83±9.3830.70±1.4052.50
UC Fine-Tuned65.33±1.0171.70±0.0683.53±3.2732.93±1.3763.37

(R3) Graph regression performance and more graph-level benchmarks (ZXUN, 5UEq, uopr)

Upon exploring the EC 7 and 10 datasets, we found that UC and many baselines have RSE around 1.0 due to labeling issues in those splits - that is, many circuits labeled as invalid (label -300.0) have the same distribution of input features and graph topologies as valid (labels in [-5, 5]), and there is no other signal to properly distinguish between valid and invalid circuits. Invalid circuits with such labels pollute the dataset and should be cleaned, we contacted the original dataset authors about this matter.

Having said that, the updated results on EC graph regression splits (RSE ↓\downarrow with std) demonstrate strong UC capabilities:

DatasetRidge RegressionKNNRFGBDTGINUC Zero-ShotUC Fine-Tuned
EC-5 EFF0.7600.7780.7520.7200.8400.7422±0.01050.4715±0.0062
EC-5 VOUT0.7600.7830.7510.7240.8560.7285±0.01190.5202±0.0186
EC-7 EFF0.9701.0090.9880.9890.9120.9192±0.05060.9197±0.0725
EC-7 VOUT0.8971.0010.9260.8900.9370.8960±0.01060.8643±0.0302
EC-10 EFF0.8930.9350.8890.8770.8310.8250±0.03070.6849±0.0453
EC-10 VOUT0.9481.0530.9520.9770.9260.9001±0.01830.8082±0.0087
Avg.0.87130.92650.87630.86280.88370.83520.7115

As requested by reviewers, we add more graph-level tasks.

Regression on GraphBench Max-Flow datasets (MAE):

MAE ↓\downarrowGINGCNUC Zero-ShotUC Fine-Tuned
Flow-Easy3.444.491.65±0.141.18±0.01
Flow-Med9.608.560.96±0.020.76±0.00
Flow-Hard9.518.910.96±0.030.76±0.00
Avg.7.527.321.190.90

Classification on TUDatasets (Accuracy) and OGBG (ROC AUC)

DatasetGINUC Zero-ShotUC Fine-Tuned
PROTEINS (TUDataset)73.364.81±5.0375.23±0.34
IMDB-B (TUDataset)71.265.40±5.7174.43±0.64
IMDB-M (TUDataset)48.539.56±6.2351.16±0.56
MolBACE (OGBG)72.9769.24±1.4779.08±3.81
Avg.66.4959.7569.98

(R4) Baseline tuning (ZXUN), baselines are weaker than published results performance (uopr)

All baselines were taken from their respective papers [GraphAny, TS-Mean, NodePFN], qualifying text claims. Specifically, Table 4 used results taken from GraphAny. We will revise the specific result you pointed out and use the ones from Platonov et al. Please note that we did not claim UC to outperform specialized bespoke GNN architectures tailored for specific datasets. Instead, we mainly compare against other generalist models, and zero-shot UC leads when on all 5 sets:

Dataset (Acc %↑\uparrow)SAGEGATGCNGraphAnyTS-MeanNodePFNUC Zero-ShotUC Fine-Tuned
roman-empire85.7480.8773.6963.3466.36—78.94±0.4182.10±1.05
amazon-ratings53.6349.0948.7042.8042.2744.6853.06±0.2455.16±0.16
ogbn-arxiv71.4973.6571.7458.8556.33—67.00±0.6670.65±0.06
full-dblp—73.8773.0271.4866.4274.7185.23±0.1085.48±0.20
full-cora—58.9561.0651.1853.58—70.28±0.3970.32±0.20

(R5) Model and Data Ablations, robustness (ZXUN, 5UEq)

The pre-training mixture consists of 30% node classification, 40% node regression, 30% link prediction (we don’t train on graph tasks specifically) on graphs with up to 200k nodes, 10M edges, 10000 features, 100 classes (32 regression bins for regression). We believe the parameter count is not that informative when techniques like MoEs enable massive models but FLOPs depend on active parameters. Therefore, we treat FLOPs as a more informative measure. A single training UC run takes about 2e+172e+17 FLOPs.

To test mixture sensitivity, we ran more ablations measuring performance on our suite of node/link/graph-level tasks: removing link prediction from the mixture harms every regime. We haven’t found a significant performance difference when all tasks are present but in slightly different proportions (eg, 40% classification, 40% regression, 20% link prediction). Thank you for prompting this analysis, we will update the text accordingly.

Ablation Variant13 Node Cls8 Node Reg (R2R^2)4 LP, Hits@106 EC (RSE ↓\downarrow)
UC70.2869.7482.340.82
No GNN layers−20.75−58.44−48.54+0.34
No Transformer layers−10.81−42.29−13.44+0.29
No anchor self-attention−5.65−34.72−10.44+0.31
6 Transformer layers−38.48−85.51−59.14+9.48
Node-level only (43% classification / 57% regression)−5.47−31.99−29.84+0.25
Link-prediction only−22.12−96.84−16.64+1.00

To test whether gains reflect genuine in-context graph inference rather than feature memorization, we ran 3-seed inference interventions isolating the GNN propagation and test-time anchor labels:

Label/edge perturbations (Acc / R2R^2 ↑\uparrow)

Intervention (3 Seeds)13 Node Cls4 GraphLand Cls3 GraphLand Reg (R2R^2)
Base UC70.37±0.0969.39±0.2467.47±0.04
No neighboring labels60.87±1.2862.47±0.5567.92±0.05
No edges52.82±0.9056.75±0.6267.51±0.02
Test anchor labels permuted33.52±1.1641.80±1.7851.00±1.44

Removing edges or removing neighboring labels (known from the training set) during message passing substantially hurts classification performance while regression is more robust. However, permuting anchor labels collapses both classification and regression. This rules out shortcut feature memorization: predictions in both regimes depend causally on true in-context anchor labels.

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