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Under review as a conference paper at ICLR 2027

A Generative Model of Complex Networks Using Graphons and Neural Inverse Operators

Abstract

Generative graph models are central to understanding and simulating complex networks. However, existing approaches have complementary strengths and limitations. Mechanistic models offer interpretability but rely on instance-specific estimation methods. Deep generative models, on the other hand, offer amortized inference at the cost of interpretability and are largely limited to graph sizes seen during training. Scientific applications motivate a framework that retains the strengths of both paradigms. We bridge them by formulating both the generative model and parameter recovery in function space. A multifractal step graphon extends standard step graphons with a recursive construction that compactly parameterizes complex networks. This formulation admits a neural inverse operator to recover its parameters, enabling inference on unseen graph sizes. We evaluate our model, trained only on synthetic multifractal step graphon realizations, against both paradigms. Against a graph foundation model pretrained on empirical networks, our method achieves the best average performance on three of four metrics in a zero-shot graph-generation benchmark, indicating that the model transfers to real-world graphs. We also apply our method to single-observation networks, a regime largely inaccessible to deep models that require training corpora, where it performs comparably to an instance-specific method that optimizes on each graph. In a multi-subject EEG case study, the inferred parameters track a reversible change in brain state more sensitively than traditional network statistics. Together, these results indicate that mechanistic interpretability and amortized inference can be effectively unified in a generative graph model to enhance our understanding of complex networks.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
complex networks, generative graph models

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_1qVrOpenReview ↗
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3
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3
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3
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Paper summary

The paper proposes a multifractal step-graphon model that represents multiscale network-generation rules through a recursive Kronecker structure, together with a Multi-Wavelet Neural Operator Transformer (MWNOT) that amortizes recovery of base parameters from an observed adjacency matrix. It provides an identifiability proposition under specific non-degeneracy conditions, with recovery defined up to community-label permutation. It also evaluates parameter recovery at unseen network sizes, zero-shot generation on real networks, reconstruction from a single observed network, and an application to multi-subject EEG state analysis. The main assessment questions concern the scope of the assumptions and the extent to which population-level identifiability translates into stable recovery from finite, noisy network observations

Critical strengths

(1) An interpretable generative model paired with amortized inference. The multifractal step graphon represents multiscale connection rules through a recursive Kronecker structure, while the neural inverse operator estimates base parameters, giving the paper a coherent generation-to-inversion pipeline. (2) Complementary theoretical and empirical evaluations. The paper provides a conditional identifiability result and studies parameter recovery at unseen network sizes, zero-shot generation across empirical network domains, single-network reconstruction, and an EEG state-analysis applicatio

Critical weaknesses

(1) The identifiability result should not be conflated with finite-sample recovery guarantees. The proposition establishes identifiability of base parameters, up to community-label permutation, under specific positivity and non-degeneracy conditions. It does not automatically guarantee stable parameter estimation from a single finite and noisy graph. The gap between population-level identifiability and practical amortized recovery deserves clearer discussion. (2) The recursive cross-scale assumption limits the range of networks to which the model naturally applies. The paper evaluates transfer to unseen network sizes and zero-shot generation on empirical networks, but it also relies on a repeated connection rule across scales and deterministic degree-order normalization. Reported weaknesses on some domains and spectral metrics suggest that applicability to networks departing from the assumed multifractal structure should be delineated more clearly.

Questions for authors

(1) Proposition 1 establishes identifiability up to community-label permutation under specific non-degeneracy conditions. How does this population-level result relate to parameter recovery from a finite, single observed network? Which sources of error or violations of assumptions are most likely to make practical recovery unstable? (2) The paper evaluates unseen network sizes from N=128 to N=8192 and zero-shot generation across empirical network domains. Given the assumption that the same connection rule repeats across scales, how should applicability be characterized for networks that do not follow this recursive structure? Which network characteristics are most associated with the remaining spectral-metric errors?

4 comments
AuthorsOpenReview ↗

Summary of the Response

Thank you for the careful review, and for the two questions that pushed us to test the method harder. We ran four new experiments with the frozen model of the paper (no retraining) to answer with numbers.

For the reviewer's convenience, we restate our work: our framework bridges the interpretability of mechanistic graph models with amortized inference of deep generative models. Two properties make it readily applicable for scientific applications. First, one model transfers to empirical networks across many domains and returns the rule in a single forward pass after pre-training only on synthetic graphs generated by our multifractal step graphon. Second, the model and the inference are formulated in function space, allowing generalization to unseen network sizes. Critically, this practicality does not come at the cost of accuracy, as our model's performance is comparable to a per-network optimization method within the same model class.

The implication is that a practitioner needs only one model to extract the mechanistic generative rule of empirical networks of various domains and sizes. Each rule can then be used for downstream applications, such as hypothesis testing and controlled perturbations in forward simulations, network control, and settings where only a single network is observed. As such, we believe that our method has the potential to greatly enhance our understanding of complex networks.

We summarise our response here, with details for each below. We hope that the discussion here clarifies the reviewer's concerns. If so, we respectfully ask the reviewer to consider this in the final assessment.

  1. (Q1a) Identifiability and finite recovery. We split the recovery error into bias and graph-to-graph spread. The spread vanishes as the graph grows (0.025 at N = 512 to 0.004 at N = 8192 on p), so two graphs from the same rule give almost the same estimate. More than 90% of the squared error may be a consistent bias of the trained network. Since Proposition 1 guarantees that an exact inverse exists, the limitation is in the trained network and not in the formulation. We note that the main contribution of our paper is the overall formulation of the generative prior and inference in function space, with MWNOT serving as one instance of the architecture. The remaining bias is therefore something that better training and architectures can reduce, without any change to the formulation.

  2. (Q1b) Sources of instability. This is a great question. We ran experiments to seek the answer. The results indicate that the main source is too few nodes per block. We note that this is a property of any block model, since block parameters cannot be estimated from a handful of nodes. Training on larger graphs would allow greater depths while keeping enough nodes per block. This serves as an interesting direction to explore for scaling up our method.

  3. (Q2a) Applicability beyond the recursive assumption. We also found this question interesting, as we acknowledged in the discussion that this is an assumption of our model. To test this, we ran a new experiment in which the rule differs across scales. The results show that Recovery is as accurate as with exact repetition at eps = 0.05, where each level differs from the base rule by about 0.025. At eps = 0.1, where the levels differ by about 0.05, the error on p is 6% higher and the error on l is unchanged, and it degrades gradually beyond that. The method is therefore not strictly constrained to networks that follow the assumption exactly. However, this assumption is also something we are working on loosening more in the future. Therefore, the reviewer raises an important point.

  4. (Q2b) Remaining spectral error. Our new experiments indicate that the error is concentrated in sparse networks, with a correlation with mean degree of -0.91 across domains and -0.49 within domains. This draws a measurable boundary for the applicability of the method. The error is not tied to cropping or to depth selection, which supports these design choices. It also points to a concrete extension, such as a generative prior that can better infer the rule from sparse networks.

Q1a. "How does this population-level result relate to parameter recovery from a finite, single observed network?"

Here we measured the gap from theory to practice that the reviewer pointed out. We fixed 20 rules, drew 50 graphs from each at three sizes (K = 4), and split the error of the estimate into two parts. Bias is the distance between the average estimate and the truth. Spread is the standard deviation of the estimate from graph to graph.

NBias, pSpread, pBias, lSpread, l
5120.0800.0250.0680.030
20480.0960.0100.0850.014
81920.1030.0040.0880.006

The spread shrinks as the graph grows: at N = 8192, two graphs from the same rule give almost the same estimate. The bias stays, and it makes up more than 90% of the squared error at every size. So the model's error is consistent, not random. Proposition 1 guarantees that an exact inverse exists. The limitation is therefore in the trained network, not in the formulation. This suggests that future studies improving the training and architecture of the network can further mitigate this.

Q1b. "Which sources of error or violations of assumptions are most likely to make practical recovery unstable?"

In short: too few nodes per block. A depth-K graphon has 2^K blocks, so what matters is the combination of N and K, that is N / 2^K. We reran the Figure 4 protocol and kept the error of every graph (4,000 graphs, N = 128 to 8192). Mean absolute error:

Nodes per block, N / 2^K2-44-1616-6464-256256-10241024-4096
Error on p0.1470.1060.0890.0850.0800.078
Error on l0.1300.0970.0770.0690.0550.046

Below about 16 nodes per block the error rises. Above that, recovery is stable: the error on p stays between 0.085 and 0.089 from N = 256 to N = 8192, eight times the largest training size.

We note that this is a property of any block model. Block parameters cannot be estimated from a handful of nodes. Appendix A (lines 762-768) already stated this constraint. These results help us quantify it. In addition, every graph with N ≥ 1024 meets it at any depth the method selects (K ≤ 6).

Q2a. "Given the assumption that the same connection rule repeats across scales, how should applicability be characterized for networks that do not follow this recursive structure?"

Applicability can be assessed with a fit check on each network. The paper states this assumption as a limitation (lines 477-479) and gives a check for it in the EEG case study (Appendix K of the submitted version, lines 1447-1463; Appendix L of the revised version). We infer the rule, generate networks from it, and compare the reconstruction error with its range on synthetic networks for which the model is true. A network passes if its error is below the 95th percentile of that range. Of the 80 EEG networks, 76 pass.

We also quantified what happens when the assumption fails. The main takeaway is that the method tolerates mild departures from it. For the table below, we generated graphs in which each of the K = 4 levels uses its own perturbed copy of the base rule, with independent noise of size eps, and compared the recovered rule with the base rule (N = 1024, 1,000 graphs per eps, mean ± standard deviation over 10 seeds).

epsChange of the rule per level, p / lMean absolute error, pMean absolute error, l
00 / 00.080 ± 0.0040.068 ± 0.008
0.050.025 / 0.0180.081 ± 0.0040.066 ± 0.007
0.10.049 / 0.0370.084 ± 0.0040.068 ± 0.008
0.20.095 / 0.0740.103 ± 0.0050.084 ± 0.009
0.40.177 / 0.1460.153 ± 0.0070.124 ± 0.014

At eps = 0.05, where the levels differ by about 0.025 on average, recovery is as accurate as with exact repetition. At eps = 0.1, where they differ by about 0.05, the error on p is 6% higher and the error on l is unchanged. Beyond that the error grows gradually and roughly doubles at eps = 0.4.

Q2b. "Which network characteristics are most associated with the remaining spectral-metric errors?"

The analysis below shows that sparsity is most associated with the remaining spectral-metric errors. For the 548 unique reference graphs of the 12 domains, we correlated the spectral error (Table 1, test graph as input) with properties of each reference graph and with the selected depth, all fixed before the analysis. Spearman correlations with 95% bootstrap intervals. We show the main rows here; the full list of ten properties is in Table S9 (Appendix N.4, p. 34):

PropertyAcross domains (n = 12)Within domains (n = 548)
Mean degree-0.91 [-1.00, -0.57]-0.49 [-0.70, -0.22]
Average clustering-0.40 [-0.89, 0.35]-0.40 [-0.63, -0.14]
Fraction of nodes cropped-0.13 [-0.68, 0.63]0.07 [-0.25, 0.38]
Selected depth K*-0.10 [-0.83, 0.61]-0.18 [-0.42, 0.04]

The error is higher for sparser networks, and we detect no association with cropping or with the selected depth. The remaining spectral error is therefore concentrated in sparse networks, and it is not tied to cropping or to depth selection. We note that this is a known limit of graphon models, which describe dense graphs best. This provides an interesting way to extend the model prior for future studies.

AuthorsOpenReview ↗

Final Comment

We sincerely thank the reviewer again for their questions and insights. We also apologize for the additional comment, and we hope the reviewer can understand that we write it out of our commitment to this work.

We highlight two of the new results that address the reviewer's concerns. The details are in our response above.

  • The method holds beyond exact recursion (Q2a). When the rule differs across scales, recovery is as accurate as with exact repetition at eps = 0.05. At eps = 0.1, the error on p is only 6% higher and the error on l is unchanged.
  • The design choices are supported (Q1b, Q2b). The remaining error is not tied to cropping or to depth selection.

We would be very grateful if the reviewer could consider these results in the final assessment.

Reviewer_y7BeOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper bridges mechanistic interpretability and amortized inference in graph generation by proposing a multifractal step graphon via recursive Kronecker expansion. Parameter recovery is cast as an inverse operator-learning problem solved by a Multiwavelet Neural Operator Transformer (MWNOT) on degree-sorted adjacency matrices. Experiments show zero-shot transfer across 12 domains, fast single-graph reconstruction, and brain-state tracking in EEG networks.

Critical strengths

S1. Bridging mechanistic graph models with neural operator learning is a well-motivated direction.

S2. The model is lightweight (∼205K\sim 205\text{K} parameters) and achieves much faster inference on single-observation networks than per-instance EM optimization.

S3. The paper is well-structured, and Figure 1 provides an intuitive overview of the framework.

Critical weaknesses

W1. The authors use degree sorting to achieve permutation invariance, claiming that expected degree is monotone in community membership (Appendix E.1). However, by Eq. (S3), block expected degree E[dqout]=Nc0K−∣q∣c1∣q∣\mathbb{E}[d_q^{\text{out}}] = N c_0^{K - \vert{}q\vert{}} c_1^{\vert{}q\vert{}} depends only on the Hamming weight ∣q∣\vert{}q\vert{} rather than the lexicographical order on [0,1][0, 1]. Thus, all (Kw)\binom{K}{w} blocks with the same Hamming weight share identical expected degrees, causing degree sorting to interleave nodes across blocks and scramble the recursive dyadic boundaries required by the wavelet basis.

W2. To fit the 2D multiwavelet transform, non-dyadic graphs are cropped to 2⌊log⁡2N⌋2^{\lfloor \log_2 N \rfloor} by dropping the lowest-degree nodes (Appendix D.1), discarding up to nearly 50%50\% of vertices (e.g., 42%42\% in Drosophila and 30%30\% in EEG). Since low-degree nodes govern the q<0q < 0 tail of the multifractal spectrum (Appendix J.1), excising the periphery biases θ^(1)\hat{\theta}^{(1)} and degrades global spectral metrics (SpecW). Moreover, Figure 4a only tests exact powers of two, masking this cropping error.

W3. In Table 1, unlike LGGM-X and DiGress which generate graphs without accessing individual test instances, Ours feeds each held-out test graph into MWNOT to infer per-instance θ^(1)\hat{\theta}^{(1)} and uses its exact edge density ρemp\rho_{\text{emp}} to solve for K⋆K^\star (Appendix H). This is per-instance reconstruction rather than unconditioned generation, which explains why even the trivial ablation Ours-Mono (p(1)≡0.5p^{(1)} \equiv 0.5) beats DiGress on all metrics.

W4. The paper lacks comparisons with critical baselines in both niches to justify its design. It neither compares against neural graphon or Kronecker estimators, nor ablates non-wavelet operator backbones (e.g., FNO or ViT/MLP on sorted matrices) to verify the necessity of MWNOT. It is suggested to compare or discuss relevant research, such as,

[1] Xia, Xinyue, et al. "Implicit graphon neural representation." AISTATS. PMLR, 2023.

[2] Reza Ramezanpour, et al. "A Few Moments Please: Scalable Graphon Learning via Moment Matching." NeurIPS, 2025.

[3] Li, Zongyi, et al. "Fourier neural operator for parametric partial differential equations." ICLR. 2021.

Questions for authors

Q1. How much detail-coefficient energy (Appendix E) is actually preserved when evaluating on degree-sorted finite realizations under Hamming-weight shell mixing?

Q2. How does recovery MAE in Figure 4a behave on non-dyadic graph sizes, and can interpolation mitigate the peripheral truncation bias?

Q3. In Table 1, how does the model perform under a fair unconditioned setup where θ^(1)\hat{\theta}^{(1)} and K⋆K^\star are estimated solely from the training/validation split?

Q4. Can the authors provide an ablation replacing the multiwavelet basis with FNO [3] or an MLP/ViT, and compare against graphon/Kronecker baselines [1, 2]?

9 comments
AuthorsOpenReview ↗

Summary of the Response

We sincerely thank the reviewer for their comments. We are encouraged that the reviewer found the problem "well-motivated," recognizes the value in the comparison with direct fitting methods, and finds the paper "well-structured."

For the reviewer's convenience, we restate our work: Our framework bridges the interpretability of mechanistic graph models with amortized inference of deep generative models. Two properties make it readily applicable for scientific applications. First, one model transfers to empirical networks across many domains and returns the rule in a single forward pass after pre-training only on synthetic graphs generated by our multifractal step graphon. Second, the model and the inference are formulated in function space, allowing generalization to unseen network sizes. Critically, this practicality does not come at the cost of accuracy, as our model's performance is comparable to a per-network optimization method within the same model class.

The implication is that a practitioner needs only one model to extract the mechanistic generative rule of empirical networks of various domains and sizes. Each rule can then be used for downstream applications, such as hypothesis testing and controlled perturbations in forward simulations, network control, and settings where only a single network is observed. As such, we believe that our method has the potential to greatly enhance our understanding of complex networks.

We summarise our response here, with details for each below. We hope these changes resolve the concerns raised. If they do, we would kindly ask the reviewer to consider this in the final assessment. We are happy to answer any further questions.

  1. (W3, Q3) Table 1. We contextualize our zero-shot inference with existing foundation models that also perform single-pass on test input after pre-training only on synthetic data. We also clarify our intention for this comparison as serving as context for transfer to unseen empirical graphs and showing the broad applicability of the approach. To achieve this, we test our method in a recent zero-shot whole-graph reconstruction benchmark. Despite similar performance as a larger model pre-trained on thousands of empirical data, we never position our work to be a graph foundation model because our goal is to simply have a context for our model’s zero-shot reconstruction performance (lines 405-406, line 472). We revised the manuscript to avoid phrasing such as “outperforms” and more plainly compares the performance as having “lower error” (Abstract; Sec. 5.3.1, pp. 8-9). We also ran the requested experiments. Table 1 (p. 8) now states what each method receives, with the protocol in Appendix I (p. 24) and per-domain values in Table S2 (p. 25). As requested by the reviewer, we also inferred the rules from training graphs only, so the model has no access to the test graphs. It still has a lower error than LGGM-X on ¾ metrics, averaged across all domains. We added WMGM as requested by 2kHy, which performs direct fitting on each test graph for our model class. Our model matches it on the clustering metric and has a lower error on the other three metrics. These results show that our framework transfers to empirical networks from many domains, which supports its broad applicability.

  2. (W1, Q1) Degree sorting. We measured the detail energy as requested. For rules from the training prior, the degree-sorted input carries the same detail energy as the ideal ordering by true block index, within 0.0041 at every depth. Degree sorting therefore does not remove the multiscale signal that the operator uses, and recovery on sorted inputs is accurate. We thank the reviewer for this question that helped us push our method further.

  3. (W2, Q2) Non-dyadic sizes. Nearest-neighbour resampling down to the largest dyadic size, as the reviewer suggested, returns the recovery error to the dyadic level with no retraining. While effects on the downstream results are minor (Table 1: the degree, clustering and spectral errors change by at most 0.003), we believe that this is a useful insight provided by the reviewer and incorporated this result into the appendix (Appendix M, Tables S4 and S5, pp. 31-32).

  4. (W4, Q4) Baselines and backbone. We ran the requested ablation. The error of the multiwavelet transform is 1.5 to 2.4 times lower than that of a Fourier basis at every depth at N = 4096 (1.0 to 1.6 times at the training sizes), with a matched number of parameters.This is empirical evidence that the multiwavelet basis provides a suitable inductive bias for this inverse problem. We also note that the contribution of our paper is the formulation. We present MWNOT as one instance of the inference method, not as the optimal one (lines 297-298, 476-477). We do agree with the reviewer further exploration in this direction may be interesting in the future.

W3. In Table 1, unlike LGGM-X and DiGress which generate graphs without accessing individual test instances, Ours feeds each held-out test graph into MWNOT to infer per-instance and uses its exact edge density to solve for (Appendix H). This is per-instance reconstruction rather than unconditioned generation, which explains why even the trivial ablation Ours-Mono () beats DiGress on all metrics.

We are happy to clarify. Our model is pre-trained only on synthetic graphs generated by our multifractal step graphon. At test time, it performs a single forward pass on the observed graph, with no re-training or fine-tuning. This is a paradigm seen in other zero-shot approaches of the prior-fitted networks. TabPFN [1] (tabular prediction), ForecastPFN [2] (time-series forecasting) and GraphPFN [3] (node-level prediction on graphs) follow this paradigm. Each is pre-trained on synthetic data and applied zero-shot to unseen real data.

Our intention for Table 1 was to show that our generative prior and our inference transfer to empirical graphs from many domains. We therefore used an existing benchmark designed to test transfer across domains for whole-graph generation. LGGM-X generates whole graphs. GraphPFN [3] predicts node-level targets. Ours infers the generative rule of a whole graph. Therefore, LGGM-X is the closest available reference at the whole-graph level for generalization. As published, LGGM-X is an unconditional sampler. It generates graphs for a domain from noise and has no mechanism to take a graph as input. We emphasize that the paper presents the comparison as “reference points for transfer and fit” (lines 472-473), not a competing graph foundation model, which is not the focus of this paper. In this way, we believe that the comparison against LGGM-X is still useful.

"This is per-instance reconstruction rather than unconditioned generation, which explains why even the trivial ablation Ours-Mono beats DiGress on all metrics." We respectfully disagree. The DiGress values come from Table 2 of [4]. There, DiGress is trained on QM9, a benchmark of small molecules, and applied zero-shot to each held-out domains, such as BIO, POWER, ECON, FB, etc. It serves as an out-of-domain control for LGGM-X, which is pre-trained on thousands of empirical networks outside the held-out domain X. That Ours-Mono improves on a model trained on molecules is therefore not evidence of a flaw in the evaluation. The relevant reference is LGGM-X, and Ours-Mono falls behind it on three of four metrics averaged across domains.

"uses its exact edge density to solve for K (Appendix H)"* We clarify the two stages of our method. The first is the inverse step. The operator maps a graph to the generative rule parameters in one forward pass, with no per-graph optimisation. The edge density is not used here.

The second is the forward step. The generative model produces a graph from the base parameters at a chosen size N and depth K. N and K are parameters of the forward model, not part of the inference. Any K can be chosen. We set K by matching one observed moment, the edge density, through the closed-form relation of Appendix B. This follows moment-based estimation for Kronecker graphs [5], and it parallels the standard practice of fixing the graph size from data before sampling [6]. Crucially, no evaluation metric is computed or minimised to choose K.

[1] Hollmann, Noah, et al. “Accurate predictions on small data with a tabular foundation model.” Nature, 2025.

[2] Dooley, Samuel, et al. “ForecastPFN: Synthetically-Trained Zero-Shot Forecasting.” NeurIPS, 2023.

[3] Eremeev, Dmitry, et al. “GraphPFN: A Prior-Data Fitted Graph Foundation Model.” ICML, 2026.

[4] Wang, Yu, et al. “A Large-Scale Training Paradigm For Graph Generative Models.” ICLR 2025.

[5] Gleich, David F., and Art B. Owen. "Moment-Based Estimation of Stochastic Kronecker Graph Parameters." Internet Mathematics, 2012.

[6] Vignac, Clément, et al. "DiGress: Discrete Denoising Diffusion for Graph Generation." ICLR, 2023.

Q3. How does the model under a fair unconditioned setup where the parameters are estimated solely from the training/validation split

The reviewer asked how the model performs when the rule and K* are estimated only from the training or validation split. We ran this experiment (rows B in the table below). For each generated graph, we draw one training graph of the domain, infer the base parameters and K* from it, and sample a graph of its size. No test graph is used at any stage.

DegreeClusteringSpectralOrbit
A DiGress0.31120.56220.20300.5923
A LGGM-X0.14080.34220.12530.2616
B Ours0.0908±0.01030.1492±0.01010.1060±0.00780.3005±0.0258
C Ours0.0895±0.00370.1519±0.00750.1057±0.00350.2759±0.0114
B Ours-Mono0.1984±0.01470.2805±0.02080.1594±0.00620.3678±0.0249
C Ours-Mono0.1950±0.00270.2785±0.01110.1584±0.00190.3632±0.0114
D WMGM0.1155±0.00770.1554±0.01030.1269±0.00470.3443±0.0150

ALL rows: mean over 12 domains, lower is better. A: published values. B–D: mean ± standard deviation over 10 seeds. A – Out-of-domain, unconditional B – Pretrained on synthetic graphs. Rules inferred zero-shot from the domain’s training graphs. Generated networks compared against test graphs. C – Synthetic pretraining. Zero-shot rule inference on the test graph, evaluated on the same graph. D – optimised on each test graph.

The main trend holds. Averaged across domains, Ours under both contexts (B and C) has a lower error than LGGM-X on 3/4 metrics, matches WMGM on the clustering metric, and has a lower error than WMGM on the other three. The takeaway is that a prior and an inference method trained only on synthetic graphs transfer to real networks. Their error is comparable to that of empirical pre-training (LGGM-X) and of per-graph fitting (WMGM), with or without access to the test graph. In the revised manuscript, Table 1 (p. 8) states what each method receives (sections A to D) and reports our model under both contexts, together with WMGM (protocol in Appendix I, p. 24; per-domain values in Table S2, p. 25). The text now presents these errors as context for transfer, not as a ranking (Abstract; Sec. 5.3.1, pp. 8-9).

Reviewer_hMVcOpenReview ↗
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2(+1)
Confidence
2
Informativeness
2
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1
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Paper summary

This paper proposes an interpretability method for the graph generative setting. The proposed approach consists of assuming a multifractal step graphon to model a graph generative process, whose parameters l(1)∈ΔM−1l^{(1)} \in \Delta^{M-1}, Δ\Delta denotes the simplex, and p(1)∈(0,1)M×M\mathbf{p}^{(1)} \in ( 0,1 )^{M \times M} control the length of each block of the graphon and the value of the graphon between corresponding blocks. The proposed method seeks to recover these parameters by training on pairs of adjacency matrices and corresponding parameters of the graphon that generated such adjacency matrix. At inference time, given a graph, we can get an estimate for the values of the parameters for the assumed graphon-based generative process. The recovered values for these parameters enable more interpretability over the underlying graph generative process, e.g., for graph regime identification/characterization.

The paper is reproducible: the authors provide implementation, hyperparameter details, and code.

Critical strengths
  1. The proposed method seeks to address an important question: improving the interpretability of graph generative models. The authors adopt existing ideas on multifractal network generators and formulate a learning problem to retrieve the estimates of the parameters that generated a given graph, under the assumption of multifractal network generators. These parameters are estimated via neural networks.
Critical weaknesses

My main concerns with paper subdivide into two different categories:

  1. Presentation:

    1. The paper can be significantly improved in terms of clarity of message. Understanding the method requires repeatedly navigating between sections (including the appendix) to understand how the proposed method works from end-to-end. A figure with the different steps/architecture of the method could help; additionally, clearly stating the proposed training and sampling algorithms, with the respective inputs, intermediate steps and outputs clearly stated could also be useful. There are also concepts that are immediately fed to the reader without prior introduction. For example, AA and LL are not introduced before their utilization (beginning of section 4.1) and requires the reader to infer what they are.
    2. There are scientific imprecisions in the contextualisation of the work. For example, "Variational autoencoders and diffusion-based models similarly generate graphs whose sizes are effectively limited to those observed during training". This is not true; for example, see [1,2].
  2. Experimental Protocol:

    1. Section 5.2: it's difficult to grasp how good is the reported performance in terms of MAE. Can the authors elaborate on this by providing other baselines/models? My concern is that having an average $\sim$10 percentual points error (given that each of the predicted values varies between 0 and 1) in a setting where the synthetic data follows exactly the assumed models at design time does not look too convincing. Also, would it make sense for the authors to also analyze the stability with respect to K outside of the training range? (K>6).
    2. Section 5.3.1: the comparison with the chosen baselines, to the best of my understanding, is unfair, since the proposed method and baselines operate under different information settings. In particular, both DiGress and LGGM-X do not have access to the groundtruth graph (adjacency matrix), while the proposed method does. Therefore, more appropriate comparisons would involve methods that also have access to the observed graph, such as WMGM (used in the next section) and simpler baselines (e.g., SBM fitting, etc).
    3. Section 5.3.2: the method outperforms the WMGM baseline in terms of absolute performance in 2 out of 18 settings, which weakens the empirical evidence in favor of the proposed method. While running significantly faster than WMGM, it is not clear why such speed is a bottleneck in practice, given that the main setting for the paper are single or few graph settings. Note that the baseline runs in 1-2 seconds, which does not look catastrophic for interpretability of a few graph generative processes. Can the authors elaborate on this point? Can the authors quantify the practical relevance of their efficiency gains?
    4. The main motivation of the paper appears to be the recovery of interpretable generative parameters. One of the potential applications for this method, as illustrated in the paper, is the identification of changes in network regimes. However, it is unclear what advantages this approach offers over existing methods for detecting structural changes in graphs (which directly learn to detect such changes, rather than trying to explicitly recover the underlying generative mechanism). Comparing to such methods could better contextualize the proposed method. Additionally, more broadly, beyond regime detection, the practical benefits of recovering these specific generative parameters remain unclear. Can the authors also elaborate on other potential applications of their approach?

Therefore, to the best of my understanding, the paper requires major revisions both at the presentation and at the experimental protocol levels.

Questions for authors
  1. From an early stage in the paper, the authors fix M=2M=2. Did the authors perform any sensitivity analysis on this hyperparameter? Why this value by default? Is it clear whether the reported performance comes from the expressivity of the base graphon, from hierarchical depth, or both?
  2. As noted by the authors in Section 6, the proposed approach has a strong assumption on the network generation process (multifractal step graphon). So, even if the model reconstructs certain graph statistics accurately, it does not imply that the estimated parameters correspond to actual mechanisms underlying the network. Could the authors discuss in more detail the generality of this assumption and its implications?

See "Critical Weaknesses" for the remaining questions.

[1] - Efficient and Scalable Graph Generation through Iterative Local Expansion, Bergmeister et al., ICLR 2024.

[2] - DiPhon: Diffusion on Graphons for Scalable Graph Generation, Rozada et al., NeurIPS 2026.

11 comments
AuthorsOpenReview ↗

Summary of the Response

Thank you for the direct assessment. We are encouraged that the reviewer agrees with the importance of the problem.

For the reviewer's convenience, we restate our work: Our framework bridges the interpretability of mechanistic graph models with amortized inference of deep generative models. Two properties make it readily applicable for scientific applications. First, one model transfers to empirical networks across many domains and returns the rule in a single forward pass after pre-training only on synthetic graphs generated by our multifractal step graphon. Second, the model and the inference are formulated in function space, allowing generalization to unseen network sizes. Critically, this practicality does not come at the cost of accuracy, as our model's performance is comparable to a per-network optimization method within the same model class. The implication is that a practitioner needs only one model to extract the mechanistic generative rule of empirical networks of various domains and sizes. Each rule can then be used for downstream applications, such as hypothesis testing and controlled perturbations in forward simulations, network control, and settings where only a single network is observed. As such, we believe that our method has the potential to enhance our understanding of complex networks.

We also summarise key points of response here, with additional details and responses to other concerns below. We hope these changes resolve the concerns raised. If they do, we would humbly ask the reviewer to consider this in the final assessment. We are happy to answer any further questions.

  1. (W2.2) Table 1. We contextualize our zero-shot inference with existing foundation models that also perform single-pass on test input after pre-training only on synthetic data. We also clarify our intention for this comparison as serving as context for transfer to unseen empirical graphs and showing the broad applicability of the approach. To achieve this, we test our method in a recent zero-shot whole-graph reconstruction benchmark. Despite similar performance as a larger model pre-trained on thousands of empirical data, we never position our work to be a graph foundation model because our goal is to simply have a context for our model’s zero-shot reconstruction performance (lines 405-406, line 472). We revised the manuscript to avoid phrasing such as “outperforms” and more plainly compares the performance as having “lower error” (Abstract; Sec. 5.3.1, pp. 8-9). Table 1 (p. 8) now states what each method receives, with the protocol in Appendix I (p. 24) and per-domain values in Table S2 (p. 25). As requested by Reviewer y7Be, we also inferred the rules from training graphs only, so the model has no access to the test graphs. It still has a lower error than LGGM-X on ¾ metrics, averaged across all domains. We added WMGM as requested by 2kHy, as WMGM serves as the direct fitting control for our model class. Our model matches it on the clustering metric and has a lower error on the other three metrics. These results show that our framework transfers to empirical networks from many domains, which supports its broad applicability. We do not test against a stochastic block model as it does not discover the model class we wish to learn from networks.

  2. (W2.3) Practical value of the speed-up if WMGM only takes 1-2 seconds). Per fit at one depth, as reported in the paper (Table 2), ours is 9 to 550 times faster. A full WMGM fit (described below) needs an optimization at every depth and actually takes 5.9 to 14.4 s per network, against 0.004 to 0.24 s for ours, a factor of 48 to 2552 for the full procedure over all depths. We note that this is critical for real-time applications and that speed-ups of this size are a recognised contribution of operator learning. For example, the Fourier neural operator reports 0.005 s against 2.2 s for a classical solver. Our model reaches this speed while staying better than or tied with per-network fitting on 10 of 18 comparisons. In our paper, we also specify that WMGM “serves as a reference for what direct fitting achieves, not as a competing baseline” (lines 423-424, 472-473).

AuthorsOpenReview ↗

Response to Presentation Concerns

"Understanding the method requires repeatedly navigating between sections (including the appendix)"

We followed the usual split for a paper with a 10-page limit. The main text states the model (Sec. 3), the inference method (Sec. 4, Figure 2) and the results (Sec. 5), while derivations, proofs, protocols and full tables are in the appendix (A to C for the model, D to G for the architecture, training and algorithms, H to P for the experiments).

"A figure with the different steps/architecture of the method could help" We note that Figure 2 shows the steps and the architecture of the method.

We also note that the other reviewers commented positively on the presentation. Reviewer 2kHy rated the presentation “Clear and easy to follow” and found the problem “well formulated and cleanly presented”, with “Detailed and well structured materials on related work, methodology, and experimental protocols”. Reviewer y7Be wrote that “The paper is well-structured, and Figure 1 provides an intuitive overview of the framework”, and Reviewer 1qVr described “a coherent generation-to-inversion pipeline."

"Variational autoencoders and diffusion-based models similarly generate graphs whose sizes are effectively limited ... This is not true"

We thank the reviewer for these references. We note that both papers that the reviewer cited actually state this as a limitation of deep generative models for graphs in general. Bergmeister et al. [1] divide deep graph generators into autoregressive and one-shot methods, where one-shot methods use “variational autoencoders ..., generative adversarial networks ..., normalizing flows ..., score-based and denoising diffusion models”. They then write: “neither have been shown to generalize to larger unseen graph sizes.” In addition, DiPhon [2] says of diffusion models that “even when training is feasible on small graphs, it remains unclear whether the learned generative mechanism can be transferred to larger graphs without retraining.”

Therefore, these papers are consistent with our framing - deep generative graph models in general struggle with generalization to unseen graph sizes. [1] and [2] are proposed to address this limitation, and we now write "typically limited" in the revision to reflect such exceptions (Introduction, p. 2).

Notably, we already cite papers that do focus on generalization to unseen size, but note that they do not combine interpretability of compact parameters in mechanistic models in the Related Works Section.

AuthorsOpenReview ↗

Experimental Protocol (5.2)

Sec. 5.2: "how good is the reported performance in terms of MAE, Can the author elaborate by providing other baselines/models"

We are happy to give two baselines for the mean absolute error. The first is a predictor with no information about the graph, which always outputs the prior mean. It scores 0.201 on p and 0.163 on l. Our model scores 0.075 to 0.103 on p and 0.049 to 0.091 on l across K = 2 to 6 (N = 1024, ten test sets). The error for Ours is 2.0-2.7x lower on p and 1.8-3.3x lower on l than this baseline at every depth.

The second is another model. We replaced the multiwavelet transform with a Fourier basis and trained both variants from scratch on the same data, with a matched number of parameters. The table shows N = 4096, with 100 test graphs per depth.

KMAE on p, MultiwaveletMAE on p, FourierRatioMAE on l, MultiwaveletMAE on l, FourierRatio
20.0670.1382.060.0530.1282.43
30.0610.1312.130.0500.1052.08
40.0690.1301.880.0510.1072.10
50.0850.1451.700.0810.1201.48
60.1030.1581.530.0810.1291.61
Mean0.0770.1401.820.0630.1181.87

At N = 4096 the Fourier variant has an error 1.5 to 2.4 times higher than the multiwavelet model at every depth. At the training sizes (N = 128 to 1024) the factor is 1.0 to 1.6. It still improves on the no-information baseline, which shows that the formulation works with more than one architecture. We revised the manuscript to add the no-information baseline on Figure 4 (dotted line; Sec. 5.2, p. 7) and the comparison against the Fourier basis (Sec. 5.2, p. 7; Appendix O, Table S10, pp. 34-35).

Also, would it make sense for the authors to also analyze the stability with respect to K outside of the training range? (K>6). On K > 6: this follows from our design (Sec. 3, App. A). We deliberately train on small networks (N up to 1024) and show zero-shot inference on much larger ones (Sec. 5.2). A depth-K rule divides the network into 2^K blocks, and each block needs enough nodes for its parameters to appear in the graph (Sec. 3, App. A). At our largest training size, K = 6 gives 64 blocks with 16 nodes each on average. K = 8 would give 256 blocks with 4 nodes each, and K = 10 a single node per block.

Concerns about these design choices (M = 2, depth up to 6) are further addressed by two results in the paper. First, the rule is already expressive under these design choices. Varying the base parameters alone spans distinct regimes of degree distribution, assortativity, modularity and multifractal width (Sec. 5.1, Figure 3). Second, this prior and inference trained with these design choices transfer to real networks. On the 12-domain benchmark its errors averaged over all domains are lower than DiGress and LGGM-X on the degree, clustering and spectral metrics, with or without the test graph as input (see the updated Table 1 below).

Reviewer_2kHyOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces a multifractal graphon model of complex, heterogeneous networks, with a neural inverse operator that recovers interpretable parameters from graphs without instance-specific estimation. To evaluate the model’s generalisability, the authors trained it on small synthetic graphs, then tested it on larger, unseen graph sizes and a multi-domain benchmark of real-work networks, where the model showed strong performance. To evaluate the model's interpretability, the authors applied it to a human EEG case study, where the model's inferred parameters tracked sedation-induced changes in the brain state.

Critical strengths

The problem is well formulated and cleanly presented. Detailed and well structured materials on related work, methodology, and experimental protocols are provided. The core design, which combines amortised inference with interpretable parameters in a generalisable network model is tested both theoretically and empirically through both synthetic and real-world data. The experiments cover a scientific case study, demonstrating downstream application potential. Limitations are honestly stated.

Critical weaknesses
  1. One can make a model easier to interpret by choosing a simpler parameterisation, and the parameters here (l, p) captures meaningful structural variation. The paper would benefit from a clearer explanation of what additional insights these parameters provide about empirical networks compared to the standard statistics.
  2. There might be errors in the proof C.2, although not fatal to the propositions in the main identifiability claim, the claim needs to be adjusted.
  3. Unsure about ‘zero-shot’ as the method takes a reference graph, infer generator parameters, and uses edge density for recursion depth; the sampled graphs are tested against the reference graph statistic. Could authors discuss/clarify, for table 1, what information each method receives and clarify the comparisons?
Questions for authors
  1. WMGM likewise infers a generative rule from an observed network and is already evaluated in table 2. Could it be part of table 1 benchmark for comparing generation quality when both receive the reference graph?
  2. The EEG analysis needs more careful control (table 3), where under repeated measures of 20 subjects, the tests are not paired. The processing of network metrics used here are different from that used for θ inference. Could the authors add or discuss paired controls and sensitivity to preprocessing steps (e.g., cropping)?
6 comments
AuthorsOpenReview ↗

Summary of the Response

We deeply appreciate the feedback. We are encouraged that Reviewer 2kHy appreciated the depth of the details, as well as the breadth of the theoretical and empirical tests. We are particularly glad the reviewer recognized the downstream application potential demonstrated by our case study.

For the reviewer’s convenience, we restate our work: our framework bridges the interpretability of mechanistic graph models with amortized inference of deep generative models. Two properties make it readily applicable for scientific applications. First, one model transfers to empirical networks across many domains and returns the rule in a single forward pass after pre-training only on synthetic graphs generated by our multifractal step graphon. Second, the model and the inference are formulated in function space, allowing generalization to unseen network sizes. Critically, this practicality does not come at the cost of accuracy, as our model’s performance is comparable to a per-network optimization method within the same model class.

The implication is that a practitioner needs only one model to extract the mechanistic generative rule of empirical networks of various domains and sizes. Each rule can then be used for downstream applications, such as hypothesis testing and controlled perturbations in forward simulations, network control, and settings where only a single network is observed. As such, we believe that our method has the potential to enhance our understanding of complex networks.

We summarise our response here, with details for each below. We hope these changes resolve the concerns that were raised. If they do, we kindly ask the reviewer to consider this in the final assessment. We are happy to answer any further questions.

  1. (W1) What do the parameters add beyond statistics? Our output is a generative rule, which goes beyond describing a network. Its main benefit is that we can generate new networks to run forward simulations for controlled perturbations and testing hypotheses. Further benefits, such as network controllability and robustness to partial observation, are described below.

  2. (W3, Q1) Zero-shot and Table 1. We contextualize our zero-shot inference with existing foundation models that also perform single-pass on test input after pre-training only on synthetic data. We also clarify our intention for this comparison as serving as context for transfer to unseen empirical graphs and showing the broad applicability of the approach. To achieve this, we test our method in a recent zero-shot whole-graph reconstruction benchmark. Despite similar performance as a larger model pre-trained on thousands of empirical data, we never position our work to be a graph foundation model because our goal is to provide a context for our model’s zero-shot reconstruction performance (lines 405-406, line 472). We revised the manuscript to avoid phrasing such as “outperforms” and more plainly compares the performance as having “lower error” (Abstract; Sec. 5.3.1, pp. 8-9). We also ran the requested experiments. Table 1 (p. 8) now states what each method receives, with the protocol in Appendix I (p. 24) and per-domain values in Table S2 (p. 25). As requested by Reviewer y7Be, we also inferred the rules from training graphs only, so the model has no access to the test graphs. Then the graphs generated from these inferred rules were compared to the test graphs. Under this context, it still has a lower error than LGGM-X on ¾ metrics averaged across all domains. We also added WMGM as requested, which performs direct optimization on each test graph. Our model matches it on the clustering metric and has a lower error on the other three metrics averaged across all domains. These results show that our framework transfers to empirical networks from many domains, supporting its broad applicability.

  3. (Q2) EEG analysis. We repeated the analysis with paired tests and the same preprocessing for all measures. The spectrum width Δα, calculated directly from the generative rule parameters, separates moderate sedation from all three other states (effect sizes 0.70 to 0.85). This is not the case for any of the network statistics. Therefore, we show a case study where the generative rule is more sensitive at differentiating networks than traditional statistics. This is particularly interesting, given that our rule directly characterises the complexity of a network. Complexity is known to affect information processing and dynamics on networks, which are known to differ between varying levels of consciousness!

  4. (W2) Proof. We stated the hypothesis of Step 2 as a lemma (Appendix C, Step 2, Lemma 1, p. 18). The statement of Proposition 1 is unchanged. We thank the reviewer for this chance to improve the clarity of the proof.

W1. What additional insights these parameters provide compared to traditional statistics

We are happy to provide further explanations and intuition behind the proposed mathematical framework! The key difference is that our output is a generative rule manifested across multiple scales of the network, not a descriptive statistic. Once the rule is inferred from an empirical network, we can generate new networks from it, control the network through the few parameters of the rule, and infer the rule from partial or noisy observations. Traditional statistics do not offer these. We explain each of these aspects below, and we added the first two to the EEG case study in the revised manuscript (Sec. 5.3.2, p. 10).

  1. Generative rule vs statistics. Traditional statistics are descriptive and map a network to a number. Many different networks share the same value or distributions, and partial observations of the same network can give different values (Fig. 1D-E). A generative rule is a forward model. From a few parameters, it produces networks that one can sample from, carry out controlled perturbations, and form testable hypotheses. In our model, the parameters have a closed form relationship to how a network is organised across scales (Sec. 3, App. B, lines 156, 193-198, 215). This multiscale organisation shapes information processing and dynamics on networks [1-3]. Therefore, our rule allows us to answer a variety of "what if" questions. We can change a parameter, generate networks with a different multiscale organisation, and test how their function changes. A statistic can only report what was observed.

  2. Control. In a network of n nodes modelled as a linear system, finding the smallest set of nodes that can control the whole network is NP-hard [4]. A generative rule offers another route. One controls the few parameters of the rule, not the individual nodes. [5] showed this for multifractal generating measures: the parameters of one state are adjusted so that its multifractal spectrum matches that of a target state.

  3. Partial observation. A statistic computed on an incomplete network is biased by the missing part. A rule can be inferred from the observed part, and it stays robust when the network is noisy or incomplete. [6] showed that multifractal generating rules are recovered robustly from noisy and partially observed networks.

Therefore, inferring the generative rule from empirical networks can serve as a starting point for many interesting downstream scientific applications.

[1] Gallos, et al. "A small world of weak ties provides optimal global integration of self-similar modules in functional brain networks." PNAS, 2012.

[2] Moretti, et al. "Griffiths phases and the stretching of criticality in brain networks." Nature Communications, 2013.

[3] Yang, et al. "Spiking dynamics of individual neurons reflect changes in the structure and function of neuronal networks." Nature Communications, 2025.

[4] Olshevsky. "Minimal Controllability Problems." IEEE Transactions on Control of Network Systems, 2014.

[5] Yang, et al. "Controlling the Multifractal Generating Measures of Complex Networks." Scientific Reports, 2020.

[6] Yang, et al. "Hidden network generating rules from partially observed complex networks." Communications Physics, 2021.

W3 and Q1. "Unsure about Zero-shot" and what each method receives for Table 1. We are happy to clarify. Zero-shot in our case means that our model is pre-trained only on synthetic graphs generated by our multifractal step graphon. At test time, it performs a single forward pass on the observed graph, with no re-training or fine-tuning. This is a paradigm seen in other zero-shot approaches of the prior-fitted networks. TabPFN [1] (tabular prediction), ForecastPFN [2] (time-series forecasting) and GraphPFN [3] (node-level prediction on graphs) follow this paradigm. Each is pre-trained on synthetic data and performs single-pass on unseen real data.

Our intention for Table 1 was to show that our generative prior and inference method transfer to empirical graphs from many domains. We therefore used an existing benchmark designed to test transfer across domains for whole graph generation. As published, LGGM-X is an unconditional sampler. It generates graphs for a domain from noise and has no mechanism to take a graph as input. We emphasize that the paper presents the comparison as “reference points for transfer and fit” (lines 472-473), not a competing graph foundation model, which is not the focus of this paper. Therefore, we believe that LGGM-X still serves as a useful comparison.

Following the reviewers’ requests, we ran two tests. The first asks whether our result depends on access to the test graph. Following reviewer y7Be’s Q3, we inferred our rules from the domain’s training graphs only (B).

The second asks how single-pass inference compares with per-graph optimization on the same input. Following the reviewer’s request, we ran WMGM on each test graph (D).

DegreeClusteringSpectralOrbit
A DiGress0.31120.56220.20300.5923
A LGGM-X0.14080.34220.12530.2616
B Ours0.0908±0.01030.1492±0.01010.1060±0.00780.3005±0.0258
C Ours0.0895±0.00370.1519±0.00750.1057±0.00350.2759±0.0114
B Ours-Mono0.1984±0.01470.2805±0.02080.1594±0.00620.3678±0.0249
C Ours-Mono0.1950±0.00270.2785±0.01110.1584±0.00190.3632±0.0114
D WMGM0.1155±0.00770.1554±0.01030.1269±0.00470.3443±0.0150

ALL rows: mean over 12 domains, lower is better. A: published values. B–D: mean ± standard deviation over 10 seeds. A – Out-of-domain, unconditional B – Pretrained on synthetic graphs. Rules inferred zero-shot from the domain’s training graphs. Generated networks compared against test graphs. C – Synthetic pretraining. Zero-shot rule inference on the test graph, evaluated on the same graph. D – optimised on each test graph.

The main trend stays consistent. Averaged across domains, Ours under both contexts (B and C) has a lower error than LGGM-X on 3/4 metrics, matches WMGM on the clustering metric, and has a lower error than WMGM on the other three. The takeaway is that a prior and an inference method trained only on synthetic graphs transfer to real networks. Their error is comparable to that of empirical pre-training (LGGM-X) and of per-graph fitting (WMGM), with or without access to the test graph. In the revised manuscript, Table 1 (p. 8) states what each method receives (sections A to D) and reports our model under both contexts, together with WMGM (protocol in Appendix I, p. 24; per-domain values in Table S2, p. 25). The text now presents these errors as context for transfer, not as a ranking and avoids phrasing like “outperforms” (Abstract; Sec. 5.3.1, pp. 8-9).

[1] Hollmann, Noah, et al. “Accurate predictions on small data with a tabular foundation model.” Nature, 2025.

[2] Dooley, Samuel, et al. “ForecastPFN: Synthetically-Trained Zero-Shot Forecasting.” NeurIPS, 2023.

[3] Eremeev, Dmitry, et al. “GraphPFN: A Prior-Data Fitted Graph Foundation Model.” ICML, 2026.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Final Remarks

We sincerely thank all reviewers for their time and constructive feedback. We are encouraged that the reviewers found the problem "well-motivated" (y7Be) and "well formulated and cleanly presented" (2kHy), and the framework "a coherent generation-to-inversion pipeline" (1qVr). Below we restate the problem, our method and claim, the supporting evidence, and what the revision added.

The problem. Mechanistic graph models are interpretable but must be fitted to each network separately. Deep generative models amortize inference, but they have limited interpretability and are typically limited to the graph sizes seen in training. A method that can recover explicit wiring rules, whose few parameters state how a network is built and can be varied to generate new networks and test hypotheses, while amortizing inference and generalizing to unseen graph sizes, would aid scientific applications by making such rules available for any observed network without a separate fit. We note that our generative rule directly encodes the latent hierarchical community structure and multifractality of networks, which have implications for information processing and dynamics of networks.

Our method. We formulate both the generative model and its inference in function space. This allows generalization to unseen graph sizes. The compact parameterization of the multifractal step graphon captures features of many types of graphs. Its synthetic realizations therefore serve as pre-training that transfers to empirical graphs from many domains.

Supporting Evidence:

Figure 3. The prior covers diverse topologies. Varying the base parameters alone produces distinct regimes of degree distribution, assortativity, modularity and multifractal width.

Figure 4. The inference generalizes to unseen sizes. One model trained on N up to 1024 keeps a stable error from N = 128 to N = 8192. The revision adds a no-information baseline, and our error is 2.0 to 2.7 times lower on p and 1.8 to 3.3 times lower on l at every depth.

Table 1. Do these properties transfer to empirical graphs of many domains and sizes?

  • The submitted version showed Ours achieving lower average error than LGGM-X on three of four metrics averaged over 12 domains. Our method is pre-trained on synthetic realizations of the multifractal step graphon and performs single-pass on the test graph, similar to models like TabPFN.
  • What the reviewers asked. What each method receives as input, whether the result depends on access to the test graph, and how the model compares with a method that is fitted to the observed graph.
  • What we clarified. Our model is pre-trained only on synthetic graphs and applied in a single forward pass, with no re-training or fine-tuning. Table 1 now states what each method receives, and the text reads the errors as context for transfer and not as a ranking.
  • What we added. Our model without access to the test graph, where the rule is inferred from the domain's training graphs only. WMGM, which is optimized on each test graph.
  • What the new results show. The result holds with or without the test graph. Against WMGM, our error is lower on three metrics and about equal on the fourth.
  • Implications Table 1 now compares our model with both paradigms that we aim to bridge. It has a lower error than each on three of four metrics while keeping the strengths of both, an interpretable rule and single-pass transfer. This is our intended contribution.

Comparison with a Fourier basis.

  • Our intuition. The graphon is built by applying one rule recursively, and a multiwavelet basis describes a function scale by scale. Each level of coefficients therefore corresponds to one level of the recursion.
  • Why it was not in the submitted version. Our contribution is the formulation, and we present MWNOT as one instance of it, not as the optimal architecture. We therefore supported the choice of basis with an analysis, which shows that the detail energy of the multiwavelet coefficients grows with the recursion depth (Appendix E).
  • What the revision adds. We replaced the multiwavelet transform with a Fourier basis, with matched parameters and training. The multiwavelet model has the lower error at every depth tested, by 1.5 to 2.4 times, at N = 4096.
  • Implications The ablation isolates the effect of the basis and gives direct empirical support for our choice. The Fourier variant also improves on the no-information baseline, which shows that the formulation works with more than one architecture. Comparing function-space architectures is an exciting future direction.

In summary, one model, trained once on synthetic graphs, returns an interpretable rule for networks of many domains and sizes, at an accuracy comparable to fitting each network separately. We believe this method can help uncover the multifractal structure of real networks and, consequently, deepen our understanding of complex networks.

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

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