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REVIEW 5 major objections 7 minor 28 references

An Empirical Study of Feature Selection Granularity

T0 review · 5 major / 7 minor · reviewed 2026-07-31 · grok-4.5

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Pith's one-line read Greedy recursive elimination almost always beats one-shot global ranking for the same feature-selection criterion.

desk verdict Solid paired experiment on selection granularity with a real supervised win, but the multi-metric “almost consistent” claim does not match several of their own rank diagrams. read the letter →

arxiv 2607.24145 v1 pith:O5YSJ363 submitted 2026-07-27 cs.LG

Muhammad Rajabinasab , Arthur Zimek This is my paper
classification cs.LG
keywords featureselectionrecursiveeliminationcurseofdimensionalityalgorithmicdesigngreedyimportanceempiricalstudy
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

Feature selection usually ranks every feature once on the full set and keeps the top ones. This paper asks whether noisy or redundant features can mask the true importance of better features during that single ranking. The authors re-implement five standard selectors so that the least important feature is dropped and importance is recomputed after every removal, then compare the two designs on the same criteria. Across dozens of datasets and multiple supervised, unsupervised, and model-agnostic metrics, the recursive design produces better feature subsets almost consistently. The price is higher runtime, because the selector must be run many times. The result supports the claim that the curse of dimensionality also degrades the very procedures meant to fight it.

What carries the argument

Greedy recursive elimination: at each step the current least-important feature is discarded and the base importance estimator is re-run on the remaining features, producing an elimination order that becomes the final ranking.

What would settle it

Re-run the identical head-to-head comparison on several dense or sparse datasets with thousands of features; if the recursive variants no longer improve accuracy, AUC, clustering quality or angle-difference scores relative to one-shot ranking, the central claim fails.

Watch

Extended reading notes

Core claim

When the same feature-importance criterion is applied either once globally or iteratively by removing the least important feature and re-scoring, the iterative design yields higher-quality selected subsets on nearly every evaluation metric examined. The discrepancy is largest among the top-ranked features and shrinks only as larger fractions of the feature set are retained.

Load-bearing premise

The finding is assumed to carry over from the moderately dimensional datasets used (at most a few hundred features) to the truly high-dimensional regimes where the curse-of-dimensionality argument is usually invoked.

Editorial extensions

If this is right

  • Practitioners can obtain better feature subsets from existing selectors simply by wrapping them in recursive elimination, without inventing new criteria.
  • One-shot global rankings should be treated as approximate when many noisy or collinear features are present.
  • The computational overhead of recursion becomes the main practical barrier, so batch or subspace variants become natural next engineering steps.
  • Any new feature-selection method whose scores depend on the current feature set should be evaluated under both one-shot and recursive protocols.

Reading between the lines

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

  • The same masking effect may also distort unsupervised filters and wrapper methods that were excluded from the study, suggesting a broader design principle.
  • If removing several least-important features per round still preserves most of the gain, recursive selection could become practical for much higher dimensions.
  • The result supplies a concrete reason why feature-selection stability metrics often disagree across algorithms: they may be measuring different points on a continuum of granularity rather than purely different criteria.
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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

5 major / 7 minor

Summary. The paper asks an algorithmic-design question about feature selection: does computing importance scores once over the full feature set (global/one-shot) differ from greedily removing the least important feature and re-evaluating importance at each step (iterative/RFE-style)? The authors implement five supervised selectors (Random Forest MDI, XGBoost MDI, ReliefF, LASSO, permutation importance) in both variants, evaluate them on 28 PMLB datasets across nested subset budgets (5%–100% of features) with 5-fold CV, and compare them on ACC, AUC, clustering accuracy (CLSACC), NMI, a PCA-based model-agnostic metric (AAD), ranking similarity, and runtime, using both standard average ranks and the authors' magnitude-aware rank statistic (MARS). The manuscript claims the iterative design improves feature-selection quality 'almost consistently' across metrics, at higher computational cost, and interprets this as evidence that high dimensionality also degrades the importance-estimation step itself.

Significance. The question is genuinely useful and, to my knowledge, not systematically studied: practitioners routinely choose between one-shot global importance ranking and recursive elimination, and paired evidence across five diverse selectors (tree MDI, boosting, ReliefF, LASSO, permutation) on 28 PMLB datasets with 5-fold CV is a real contribution. The supervised result — iterative variants occupying the top rank positions on ACC (Fig. 3) — is, if it holds up under paired testing, actionable guidance. The honest negative/mixed results on CLSACC and AAD are also valuable and would strengthen the paper if reported as such rather than papered over. However, the current version overclaims a cross-metric 'almost consistent' improvement that its own figures refute, and the dimensional regime studied (≤240 features) does not match the curse-of-dimensionality motivation. The contribution is salvageable and worthwhile at a re-scoped claim; it is not currently publishable as stated.

major comments (5)
  1. [§5.2, Figs. 4–7 captions] The captions of Figs. 4, 5, and 7 each state that 'Both MARS and Standard rank statistics agree on the superiority of the iterative approach,' but the displayed rankings contradict this. Fig. 4 (AUC), MARS diagram: standard XGB ranks first (9.24) and iterative XGB last (453.53); standard Permutation and ReliefF also outrank their iterative variants. Fig. 5 (CLSACC), standard-rank diagram: every standard selector ranks ahead of its iterative counterpart (Lasso 4.04 < Lasso_iter 4.36; XGB 4.84 < XGB_iter 5.32; RF 5.39 < RF_iter 5.45; ReliefF 5.75 < ReliefF_iter 6.18; Perm 6.25 < Perm_iter 7.43). Fig. 7 (AAD), both diagrams predominantly favor the standard variants of ReliefF, RF, Perm, and XGB. The body text for CLSACC is more careful ('not as consistently superior as for the supervised measure'), but the captions and the Abstract's 'almost consistently' are not supported by the paper's ow
  2. [Abstract; §5.2; §6] Related to the above: the Abstract and §6 claim the greedy design 'improves the overall feature selection quality almost consistently,' yet by my reading of the displayed rank diagrams the iterative variant is clearly superior only for ACC (Fig. 3, where the top three positions are iterative in both statistics) and for AUC under standard ranks. NMI (Fig. 6) is mixed, and CLSACC/AAD point the other way under standard ranks. Since the paper's contribution is precisely the empirical claim about granularity, the mismatch between claim and evidence is load-bearing. A revision should either (a) restrict the claim to supervised downstream metrics and explain why supervised selectors improving supervised metrics is itself the interesting (and perhaps expected) result, or (b) provide additional analysis supporting the broader claim.
  3. [§5.2 (rank analysis methodology)] The aggregate critical-difference diagrams pool all ten variants (five base selectors x two designs). This shows overall placement but never directly tests the paired comparison the paper is actually about: RF vs RF_iter, XGB vs XGB_iter, etc., across the 28 datasets. Standard practice (Demšar, ref. [8], which the paper cites) would be a Wilcoxon signed-rank test per base-estimator pair per metric. Without paired tests, statements like 'the iterative variants occupy superior rank positions' do not establish that making any given selector iterative significantly helps; a single strong base method can shift pooled ranks. This is fixable with the existing experimental output.
  4. [§4.2; §6] The motivating story is the curse of dimensionality obscuring feature-importance estimation, yet the benchmark deliberately caps dimensionality at 240 features (§4.2), with most datasets below 100. The only genuinely high-dimensional example, COIL-20 (1024 features, Fig. 1), is used as an anecdotal t-SNE illustration and is excluded from the quantitative benchmark. The exclusion rationale in §4.2 (sparse high-d data makes granular comparison difficult) is reasonable, but then the conclusion in §6 that high dimensionality degrades feature selection analogously to distance concentration is asserted, not demonstrated — the experiments show an iterative-vs-global gap in low-to-moderate dimensions, which if anything undercuts the dimensionality narrative. Either add experiments in a higher-dimensional regime or reframe the contribution as a granularity study independent of the curse-of-dimens
  5. [§1 vs §5 and Table 1] The dataset count is internally inconsistent: §1 states 'extensive experiments across 38 datasets,' §5 states '28 datasets,' and Table 1 lists exactly 28. If 10 datasets were dropped, the selection criterion must be stated; if 38 is simply wrong, correct it. As written, a reader cannot determine whether there is selection on results.
minor comments (7)
  1. [§4 vs §5] CLSACC is defined in §4 as 'Clustering Accuracy' but listed in the §5 introductory paragraph as 'Class-Weighted Accuracy.' These are different metrics; unify the terminology.
  2. [§3, Eq. (3)] Eq. (3) and surrounding text: S_0 = {1,...,n} uses n (the number of instances) for the feature index set; it should be d. Also the elimination order is stored in 'a sequence ε' but features are then described as 'appearing late in π' — ε and π are used inconsistently.
  3. [title page; Abstract; §3; §5] Typos: affiliation 'Mahematics'; §3 'might be effected' (affected); Abstract 'on the expense' (at the expense); §5.1 'two show if there is a performance difference' (to show); §5.3 'most of the times, a one-time step' is garbled.
  4. [Fig. 1] Fig. 1's t-SNE comparison is suggestive but anecdotal: t-SNE projections are stochastic and the visual 'better discrimination' is not quantified. Please label it explicitly as a motivating illustration, and note that COIL-20 does not appear in the benchmark (Table 1).
  5. [§5.2; ref. [24]] MARS (ref. 24) is a CoRR preprint by the same authors and is one of the two rank statistics used to support the central claim. This should be disclosed in the text where MARS is introduced, and the robustness of conclusions to using only standard ranks (ref. [8]) should be stated explicitly — particularly since for AUC the two statistics disagree.
  6. [§1] The statement in §2 that there is an 'absence of prior studies investigating the granularity of the feature selection process' is strong given that RFE (refs. [9, 12]) and stepwise/wrapper methods (ref. [13]) are established; the contribution is better framed as a systematic cross-method, cross-metric comparison of the two granularities rather than the first study of iterative elimination.
  7. [§4.1] Hyperparameter choices (50 estimators for RF/XGB but only 20 for the Permutation backbone; LASSO C=0.5 fixed across all datasets) are stated but not justified or sensitivity-checked. Since the Permutation variant uses a weaker backbone than RF, the RF vs Permutation cross-comparisons in the pooled diagrams are not on equal footing; a brief note suffices.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: the paper is an empirical head-to-head of two algorithmic designs on external metrics and datasets, not a derivation that forces its conclusion.

full rationale

The central claim is that greedy recursive elimination yields better feature-selection quality than one-shot global ranking of the same criterion. That claim is tested, not derived: five base selectors are run under both designs on PMLB datasets, and performance is reported primarily via standard external metrics (ACC, AUC, CLSACC, NMI) under 5-fold CV. Nothing in the methodology algebraically entails that the iterative variants must win; the ranking similarity heatmaps even document that the two designs select different features. Recursive elimination itself is a known wrapper pattern (Guyon et al., Kohavi & John), not an author-private uniqueness result. Self-citations to FSEVAL, AAD, FSDEM, and MARS supply the benchmarking harness and secondary aggregation views; they do not define the target quantities being compared and do not make the supervised gains true by construction. Overstatement of multi-metric consistency relative to some rank diagrams is a correctness/overclaim issue, not circularity. Score 0 is therefore the proportionate finding.

Assumptions & free parameters 3 free parameters · 5 assumptions · 0 invented entities

The paper is empirical. Load-bearing commitments are standard ML evaluation assumptions, the choice to study only importance-rescoring-compatible selectors, deliberate exclusion of very high-d sparse data, and hyperparameter settings fixed without sensitivity sweeps. No new physical entities; free parameters are experimental knobs, not fitted universal constants.

free parameters (3)
  • RF/XGB n_estimators=50; Permutation backbone 20 trees, 3 shuffles; ReliefF k=10; LASSO C=0.5 OvR = as listed in §4.1
    Fixed algorithmic hyperparameters that define the importance estimators; not swept. Rankings and iterative vs global gaps could shift under other settings.
  • Subset budgets {5%,10%,...,100%} and top-k similarity cutoffs {5..25%} = 5% steps; similarity at 5–25%
    Evaluation grid chosen by authors; headline ‘almost consistently better’ aggregates over this grid.
  • Maximum dataset dimensionality cutoff (~240 features) = max d=240 in Table 1
    Explicit inclusion rule that shapes the entire empirical support for the curse-of-dimensionality narrative.
assumptions (5)
  • domain assumption Feature importance from the chosen estimators remains meaningful after each single-feature deletion and can be recompared across nested subsets.
    Required for the iterative procedure in §3 (Eq. 3) to induce a total ranking; not proved, standard RFE assumption.
  • domain assumption PMLB classification datasets with 5-fold CV and downstream ACC/AUC/clustering/AAD are adequate proxies for feature-selection quality.
    §4 evaluation protocol; standard but not unique.
  • ad hoc to paper Distance-based selectors should be excluded because distance concentration would confound the granularity comparison.
    §2.1 selection criteria; narrows the method class the claim covers.
  • ad hoc to paper Sparse ultra-high-dimensional regimes are unsuitable for granular comparison because many subsets can look equally good.
    §4.2 justification for keeping d small; directly limits external validity of the curse claim.
  • domain assumption Standard rank and MARS aggregate ranks over datasets are valid for declaring method superiority.
    §5 CD/MARS analyses; MARS is author-proposed concurrent work.

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Pith. "Pith review of An Empirical Study of Feature Selection Granularity." pith.science (2026). https://pith.science/paper/O5YSJ363

@misc{pith2026260724145,
  author       = {Pith},
  title        = {Pith review of: An Empirical Study of Feature Selection Granularity},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/O5YSJ363}},
  note         = {Machine review of arXiv:2607.24145}
}
read the original abstract

Feature selection aims to identify the most informative and relevant features for a given dataset, either in terms of capturing the underlying data structure and distribution better, or with respect to the performance on a downstream task. Existing research in this area has largely focused on developing novel algorithms (in both supervised and unsupervised settings), proposing new evaluation metrics and frameworks, or benchmarking the performance of existing methods. In this work, we examine feature selection through an algorithmic design perspective. Conventional feature selection algorithms typically compute feature importance scores globally across the entire feature set and then select the top-ranked features in a single step. However, this approach raises a critical question: Can the presence of less informative (or noisy) features mask or obscure the true importance of other, more relevant features? In other words, would a recursive strategy, where features are removed one by one while re-evaluating importance at each step, yield different and potentially better results than the standard global ranking approach? To answer this question, we conduct an extensive empirical study using five diverse feature selection algorithms. We implement each algorithm under both the conventional global selection design and the greedy recursive elimination design. We then analyze the impact of this algorithmic choice, both individually for each method and collectively across all methods, on a range of standard feature selection evaluation metrics. The empirical evaluation results show that the greedy approach improves the overall feature selection quality almost consistently, albeit on the expense of higher computational cost, supporting our initial expectation that the curse of dimensionality also obscures the ways of mitigating it.

Figures

Figures reproduced from arXiv: 2607.24145 by the authors.

Figure 1
Figure 1. The projection of the COIL-20 dataset using t-SNE, presented for the full feature set, and the top 10%, selected by both the normal and the iterative greedy approach. scale ranging from 5% to 100% of the total feature count, with increments of 5%. To ensure the generalizability of the results and mitigate the risk of overfitting, we employ a 5-fold cross-validation (CV) scheme. Within each fold, we calculate the Acc… view at source ↗
Figure 2
Figure 2. Feature Ranking Similarity heatmaps for selection budgets of 5% (top), and 10%–25% (bottom row), reflecting a high amount of discrepancy between the normal approaches and their greedy counterpart. Analysis of Accuracy (ACC) Accuracy serves as the primary indicator of overall classification success. Alongside with AUC, it is the most important eval￾uation metric we use, as the feature selection methods we selected fo… view at source ↗
Figure 3
Figure 3. Comparative performance based on Accuracy (ACC). The line plot tracks the movement_libras dataset as a case study, followed by a Critical Difference diagrams over all datasets and average performance of the methods. Both MARS and Standard rank statistics agree on the superiority of the iterative approach. Only minor changes of positions observed with the inclusion of metric values in MARS. dimensionality in degradin… view at source ↗
Figures from the paper (5 more)
Figure 4
Figure 4. Figure 4: Comparative performance based on AUC. The line plot tracks the move￾ment_libras dataset as a case study, followed by Critical Difference diagrams over all datasets and average performance of the methods. Both MARS and Standard rank statistics agree on the superiority o…
Figure 5
Figure 5. Figure 5: Comparative performance based on Clustering Accuracy (CLSACC). The line plot tracks the movement_libras dataset as a case study, followed by Critical Difference diagrams over all datasets and average performance of the methods. Both MARS and Standard rank statistics ag…
Figure 6
Figure 6. Figure 6: Comparative performance based on Normalized Mutual Information (NMI). The line plot tracks the movement_libras dataset as a case study, followed by Critical Difference diagrams over all datasets and average performance of the methods. Both MARS and Standard rank statis…
Figure 7
Figure 7. Figure 7: Comparative performance based on Average Angle Difference (AAD). The line plot tracks the movement_libras dataset as a case study, followed by Critical Difference diagrams over all datasets and average performance of the methods. Both MARS and Standard rank statistics …
Figure 8
Figure 8. Figure 8: Scalability of the standard and greedy approaches. References 1. Altmann, A., Toloşi, L., Sander, O., Lengauer, T.: Permutation importance: a corrected feature importance measure. Bioinformatics 26(10), 1340–1347 (2010) 2. Amsaleg, L., Bailey, J., Barbe, A., Erfani, S.…

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