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REVIEW 4 major objections 5 minor 68 references

Call for Action: towards the next generation of symbolic regression benchmark

T0 review · 4 major / 5 minor · reviewed 2026-08-15 · deepseek-v4-flash

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Pith's one-line read The paper's central empirical claim is that no single symbolic regression algorithm dominates across all datasets, so the field should replace single state-of-the-art rankings with per-problem, multi-objective benchmarking.

desk verdict Solid SRBench update, but the headline no-free-lunch result is partly an artifact of the dataset selection. read the letter →

arxiv 2505.03977 v1 pith:W3DYZSW7 submitted 2025-05-06 cs.LG cs.NE

Guilherme S. Imai Aldeia , Hengzhe Zhang , Geoffrey Bomarito , Miles Cranmer , Alcides Fonseca , Bogdan Burlacu , William G. La Cava , Fabrício Olivetti de França This is my paper · ORCID
classification cs.LGcs.NE
keywords symbolicregressionbenchmarkingSRBenchgeneticprogrammingperformanceprofilesnofreelunchmodelcomplexityenergyconsumption
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

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

The reading

This paper sets out to modernize the community benchmark for symbolic regression (SR)—searching data for interpretable mathematical expressions—by comparing 25 methods on 24 curated datasets with 30 independent runs each. Its central empirical claim is that no single algorithm dominates across all datasets: each method wins on some problems and struggles on others, so the field should stop reporting a single state-of-the-art method. The paper also reports that, on small and noisy physics datasets with known governing equations, no SR method found an expression that strictly beat the original equation in the trade-off between accuracy and model size, and that most top-performing methods share a constant-optimization step. This matters because those findings argue for a living, standardized benchmark that maps problems to algorithms and reports accuracy, model size, and energy cost together.

What carries the argument

The argument is carried by the benchmark design plus its visualization machinery. The black-box track is built by first discarding datasets that all methods or plain linear regression already solve (training $R^2 > 0.99$), encoding each remaining dataset by row count, feature count, and the previous benchmark's algorithm-performance scores, reducing those encodings with t-SNE, and choosing the dataset nearest each of 12 k-means cluster centroids; a cap of 25% limits any one problem family. Results are read through performance profile plots—each algorithm's empirical probability of reaching any $R^2$ threshold, summarized as an area under the curve (AUC)—and a cluster heatmap that pairs per-dataset AUC with the size of the best expression. The multi-objective picture is completed by Pareto-front plots of $R^2$ against model size on the physics track and by energy-consumption estimates measured after hyperparameter tuning.

What would settle it

Re-run the same 25 methods, with the same tuning and time budget, on a much larger and independently chosen set of regression problems and check whether one method attains the best AUC on nearly every dataset; if it does, the no-domination claim collapses. The first-principles claim would be falsified by any SR method that, on several physics datasets, returns an expression at least as accurate and smaller than the published governing equation under the same protocol.

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Extended reading notes

Core claim

Under one unified protocol—25 methods, 24 datasets, 30 seeded runs, grid-search hyperparameter tuning, and a one-hour training budget after tuning—the benchmark finds that no single algorithm dominates across all datasets: the best method differs by dataset, no method fails every problem, and methods cluster into stronger and weaker groups. Among the strongest performers, almost all include a constant-optimization step (linear, gradient-based, or non-linear), which the paper identifies as a key driver of success. On the phenomenological and first-principles track, no SR method produced an expression that strictly dominated the known governing equation in the accuracy-versus-model-size trade-off, and only one method recovered one of the equations; on noisy real data, higher $R^2$ often came with larger expressions that appear to fit noise rather than the underlying law. The paper additionally reports that the most energy-hungry methods tend to be Python-based or to include inner hyperparameter tuning, while GPU-based methods did not show clearly different energy use from CPU-based ones.

Load-bearing premise

The load-bearing premise is that the 24 selected datasets represent the range of problems symbolic regression will meet; because the black-box selection uses the previous benchmark's algorithm-performance scores as clustering features, the diversity behind the 'no single winner' conclusion could inherit the old benchmark's biases rather than being a general property of the algorithms.

Editorial extensions

If this is right

  • Practitioners should match algorithm to problem rather than trust a single state-of-the-art ranking, since the best method here varies by dataset.
  • Benchmark reports should present per-dataset outcomes and at least two objectives—accuracy and model size, plus energy—because aggregate scores hide which method wins where.
  • New SR methods should build in constant or parameter optimization, the component shared by the top-scoring algorithms in this comparison.
  • A living benchmark needs standardized hyperparameter tuning, fixed time budgets, and clear deprecation rules for unmaintained methods that do not appear on any Pareto front.
  • Energy use and early termination behavior should be reported alongside accuracy, since algorithms differ widely in runtime and some stop long before their time limit.

Reading between the lines

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

  • Because the black-box selection clusters on prior algorithm-performance scores, a neutral re-selection based only on dataset statistics (rows, features, codomain, noise level) would test whether the no-domination result is robust or an artifact of the curation procedure.
  • The per-dataset winners imply a practical meta-learning route: predict the best algorithm from dataset metadata, turning the benchmark into a recommender rather than a leaderboard.
  • The difficulty of beating known physics equations suggests adding distance-to-ground-truth as an explicit metric, so recovering the exact formula is rewarded even when label noise keeps raw $R^2$ below 1.
  • Energy and runtime could be folded into a single multi-objective score; that would penalize high-accuracy methods that consume orders of magnitude more compute and reward efficiency.
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Signed reviews

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Editorial analysis

A structured set of objections, weighed in public.

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

Referee Report

4 major / 5 minor

Summary. This paper presents SRBench 2.0, an updated benchmark for symbolic regression that nearly doubles the number of evaluated methods to 25, increases independent runs to 30, and introduces 24 datasets split into a black-box track and a phenomenological/first-principles track. The benchmark uses performance-profile plots and cluster maps for visualization, measures energy consumption, and proposes community guidelines for a living benchmark, including hyperparameter-tuning standards and deprecation criteria. The central empirical claim, stated in the abstract and in Section 5.2, is that no single algorithm dominates across all datasets, which the authors use to argue for per-dataset performance reporting and problem-dependent method selection.

Significance. If the central claim holds, the paper makes a useful contribution: it provides the largest SR comparison under a unified experimental setup, ships open code and data, and offers concrete methodological innovations (performance profiles, Pareto-front visualizations, energy profiling, and a deprecation proposal). The paper is also honest about several limitations, such as the optimistic max-R2 aggregation and the incompatibility of uDSR. However, the significance is substantially tempered by the dataset-selection procedure, which uses previous algorithm performance to choose the black-box datasets, meaning that the 'no free lunch' result may be partly built into the benchmark rather than discovered from an independent sample of problems.

major comments (4)
  1. [Section 3.1] The selection of the 12 black-box datasets uses the performance of each algorithm from SRBench 1.0 as clustering features, followed by t-SNE and k-means, with the dataset closest to each centroid chosen. Since the algorithms evaluated in this paper substantially overlap with those in SRBench 1.0, this selection directly injects historical algorithm performance into the benchmark construction. The central claim that 'no single algorithm dominates across all datasets' (abstract and Section 5.2) may therefore be an artifact of choosing datasets that maximize diversity in previous performance profiles, rather than a property of the current algorithm set on representative problems. The additional cap on Friedman-derived datasets at 25% reinforces that selection is deliberately steered toward diversity. I request a control analysis: either random dataset selection, selection based only on intrinsic dataset statistics (samples, features, distribution), or a demonstration that the main conclusion is robust to alternative selection rules.
  2. [Section 3.3 / Figure 2] The performance profiles and the cluster map are built from the maximum R2 across 30 runs, which the authors call an 'optimistic perspective.' No confidence intervals or variance measures are reported for the AUC values. Because the central comparison relies on these best-case values, a single lucky run can dominate the reported performance, and the conclusion that no method dominates may not hold under mean or median aggregation. I ask the authors to report mean/median profiles alongside the max, or to provide error bars or interval estimates for the AUC values, at least for the headline comparisons.
  3. [Section 5.1 / Figure 3 / Table 2] The text states that 'uDSR was not compatible with the library during the experiments,' yet Figure 3 includes uDSR as a column and Table 2 lists it as one of the evaluated algorithms, apparently with numerical results. This is internally inconsistent. If uDSR results are missing or invalid, they should be removed from all figures and tables or explicitly marked as unavailable; otherwise readers will incorrectly count uDSR among the successfully benchmarked methods.
  4. [Section 3.4 / Section 5.1] Energy consumption is measured only after hyperparameter tuning, while the tuning budget is 6 hours per configuration compared with 1 hour for the final training run. The energy and runtime comparisons in Figure 1 and the discussion in Section 5.1 therefore exclude a large and potentially dominant part of the total computational cost. The authors should either report total energy including tuning or clearly state that the reported figures cover only the final training phase, and discuss how this affects the energy-related conclusions.
minor comments (5)
  1. [Abstract and Section 1] Several spacing errors occur in phrases such as 'acall for actionfrom' and 'Thiscall to action'; please correct these typographical issues.
  2. [Figure 2] The y-axis label 'P[R2 ≥ x]' should specify that the probability is computed from the maximum R2 over 30 runs, matching the 'max aggregation' description in the caption.
  3. [Section 3.1] The k-means step uses 12 clusters and t-SNE with two dimensions, but no details are given about the t-SNE hyperparameters, the number of k-means restarts, or the stability of the resulting selection; adding these details would improve reproducibility.
  4. [Section 5.4] The text alternates between 'first-principles' and 'first-principle' (e.g., 'some first-principle equations'); please standardize the terminology.
  5. [Table 3] The equations in Table 3 would be easier to compare to the ground-truth formulas if the ground-truth expressions were shown alongside the recovered expressions, rather than only in separate subfigures of Figure 4.

Circularity Check

1 steps flagged · score 2.0 of 10

Black-box dataset selection in Section 3.1 uses SRBench 1.0 performance profiles as clustering features, so the no-free-lunch finding is partly an artifact of the selection rule.

  1. other [Section 3.1 (dataset selection) and Section 5.2 (no-free-lunch interpretation)]
    "we created a numerical feature vector for each dataset containing the number of samples, number of features, and the performance of each algorithm tested in the SRBench 1.0. We then applied the t-SNE algorithm to reduce this metadata of the datasets to two dimensions and created 12 clusters using the k-means algorithm over the latent encodings. Finally, we picked the dataset closest to each centroid. ... The selection of datasets in Figure 3 reveals the “no free lunch” aspect of the current state of SR — there is no algorithm that performs exceptionally well on all datasets."

    The black-box track is constructed from a feature vector that directly includes the performance of every SRBench 1.0 algorithm, and the 12 datasets are chosen as the ones closest to k-means centroids of those performance profiles. The paper then presents the resulting performance diversity on this selected set as an emergent finding: no single algorithm dominates across all datasets. Because most SRBench 2.0 methods are the same as, or closely related to, the algorithms whose performances were used as clustering features, the observed spread of performance is partly inherited from the selection rule: the procedure removes near-saturated problems and maximizes diversity in algorithm performance.

full rationale

This paper is an empirical benchmark rather than a mathematical derivation, so the classic circularity pattern of one equation reducing to another does not appear. The main circularity-adjacent element is dataset selection: Section 3.1 builds the 12 black-box datasets from a feature vector that includes SRBench 1.0 algorithm-performance values, and Section 5.2 then reports that these datasets reveal the 'no free lunch' nature of current SR. Because many of the 25 evaluated algorithms overlap with the SRBench 1.0 methods whose scores were used as clustering features, the performance spread is partly an input to the benchmark construction rather than a wholly external finding. However, this is not a forced reduction: the feature vector also includes sample and feature counts, t-SNE and k-means only induce diversity of performance profiles rather than directly enforcing 'no single winner,' and the held-out 25% test split provides genuine evaluation on the selected datasets. The phenomenological & first-principles track, energy consumption measurements, and model-size/accuracy trade-offs are independent of the selection features. I therefore assign a low score of 2: a mild selection-feedback loop worth acknowledging as a limitation, but no load-bearing self-citation chain or derivation-level circularity.

Assumptions & free parameters 7 free parameters · 6 assumptions · 0 invented entities

The central claim is empirical, so the 'free parameters' are the hand-chosen benchmark protocol settings that shape the result set. None of them is fitted to force the no-dominance conclusion, but together they define the conditions under which the claim holds. The axioms are unproven background assumptions about representativeness and measurement fairness that the reader must accept to generalize from the paper's 24 datasets.

free parameters (7)
  • Dataset exclusion threshold R2 > 0.99 = 0.99
    Section 3.1 removes any black-box dataset where all prior algorithms or linear regression reach R2 above 0.99, increasing the difficulty of the test set.
  • Number of k-means clusters for dataset selection = 12
    Section 3.1 uses t-SNE plus k-means with 12 clusters to pick one representative dataset per cluster, determining which datasets appear in the black-box track.
  • Maximum share of Friedman-derived datasets = 25%
    Section 3.1 caps Friedman-derived datasets at a quarter of the black-box selection to mitigate bias identified in SRBench 1.0.
  • Hyperparameter search time budget = 6 hours
    Section 3.4 limits hyperparameter optimization to 6 hours per dataset before the 1-hour training run.
  • Training time budget = 1 hour
    Section 3.4 terminates training after 1 hour; some algorithms stop much earlier, which affects runtime and energy comparisons.
  • Number of independent runs = 30
    Section 3.3 repeats each experiment 30 times with fixed seeds; the performance summaries aggregate these runs by the maximum R2.
  • Aggregation function for AUC = max R2
    Section 3.3 uses the maximum R2 across 30 runs when computing performance profiles and AUC, an optimistic aggregation acknowledged by the authors.
assumptions (6)
  • domain assumption The 24 selected datasets are representative of the tasks where symbolic regression is used in practice.
    The no-free-lunch conclusion is generalized from this specific set of black-box and phenomenological problems.
  • domain assumption R2 on a 25% held-out test set is a valid accuracy metric for comparing algorithms across all datasets.
    Used throughout Section 4 without accounting for dataset-specific characteristics such as heteroscedasticity or outliers.
  • domain assumption SymPy node count after minimal simplification is a fair and comparable model complexity measure.
    Section 3.3 converts all models to SymPy and counts nodes, assuming this is consistent across algorithms with different internal representations.
  • domain assumption The grid search protocol with 3-fold cross-validation on 75% of the training data yields comparably well-tuned configurations for all algorithms.
    Section 3.2 applies the same grid-search wrapper to all methods; algorithms with many hyperparameters or no GridSearchCV support are not tuned in the same way.
  • domain assumption eco2AI energy estimates based on Linux CPU and memory counters are comparable across CPU-only and GPU-based implementations.
    Section 3.4 reports energy consumption using eco2AI, which may not capture GPU power draw accurately.
  • domain assumption Prior SRBench 1.0 performance metadata is a sound feature space for selecting diverse datasets.
    Section 3.1 uses these metadata as input to t-SNE/k-means; if this metadata is biased, the dataset selection inherits the bias.

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Cite this review

Pith. "Pith review of Call for Action: towards the next generation of symbolic regression benchmark." pith.science (2026). https://pith.science/paper/W3DYZSW7

@misc{pith2026250503977,
  author       = {Pith},
  title        = {Pith review of: Call for Action: towards the next generation of symbolic regression benchmark},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/W3DYZSW7}},
  note         = {Machine review of arXiv:2505.03977}
}
read the original abstract

Symbolic Regression (SR) is a powerful technique for discovering interpretable mathematical expressions. However, benchmarking SR methods remains challenging due to the diversity of algorithms, datasets, and evaluation criteria. In this work, we present an updated version of SRBench. Our benchmark expands the previous one by nearly doubling the number of evaluated methods, refining evaluation metrics, and using improved visualizations of the results to understand the performances. Additionally, we analyze trade-offs between model complexity, accuracy, and energy consumption. Our results show that no single algorithm dominates across all datasets. We propose a call for action from SR community in maintaining and evolving SRBench as a living benchmark that reflects the state-of-the-art in symbolic regression, by standardizing hyperparameter tuning, execution constraints, and computational resource allocation. We also propose deprecation criteria to maintain the benchmark's relevance and discuss best practices for improving SR algorithms, such as adaptive hyperparameter tuning and energy-efficient implementations.

Figures

Figures reproduced from arXiv: 2505.03977 by the authors.

Figure 1
Figure 1. Median energy consumption (kWh) and training [PITH_FULL_IMAGE:figures/full_fig_p005_1.png] view at source ↗
Figure 2
Figure 2. Performance plots for the black-box track, where the lines represent the probability of obtaining a given empirically [PITH_FULL_IMAGE:figures/full_fig_p006_2.png] view at source ↗
Figure 3
Figure 3. Cluster map of the Area Under the Curve (AUC) of Expected Performances across the [PITH_FULL_IMAGE:figures/full_fig_p007_3.png] view at source ↗
Figures from the paper (1 more)
Figure 4
Figure 4. Figure 4: Pareto plots for the phenomenological & first-principles track, with model sizes on [PITH_FULL_IMAGE:figures/full_fig_p007_4.png]

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Pith tools

Reviewed August 15, 2026 · model on record in the stance chip above.