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On sparse logistic-regression data, a five-test panel is more reliable and more powerful than the standard Hosmer–Lemeshow test.

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In a large simulation study, five existing goodness-of-fit tests (McCullagh, Osius-Rojek, le Cessie-van Houwelingen, Stute-Zhu, GiViTI) control Type I error and beat Hosmer-Lemeshow in power, but a real-data example shows no single test reliably catches omitted interactions.

T0 review reviewed 2026-08-01 challenge →

load-bearing objection Useful, reproducible benchmark that makes a solid case against the HL default, but the recommendation hinges on unverified implementations in the authors' own package. the 4 major comments →

arxiv 2607.16344 v1 pith:CSKU2NYW submitted 2026-07-16 stat.ME stat.AP

Benchmarking Goodness-of-Fit and Calibration Algorithms for Logistic Regression Classifiers: A Large-Scale Simulation Study under Sparse Data

Ebrahim Khaled Ebrahim , Ahmed El-Kotory This is my paper
classification stat.ME stat.AP MSC 62J12
keywords logistic regressiongoodness-of-fitcalibrationsparse dataHosmer–Lemeshow testType I errorstatistical powersimulation benchmark
verification ladder T0 review T1 audit T2 compute T3 formal T4 reserved

The pith

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

The reading

The paper asks which goodness-of-fit test a practitioner should trust when checking a logistic regression on sparse data, where continuous predictors make nearly every observation its own covariate pattern and invalidate the classical Pearson and deviance chi-square tests. Through a large simulation benchmark of roughly twenty-five tests, it claims that the ubiquitous Hosmer–Lemeshow test, while correctly sized, is mediocre in power, and that several other widely used tests are dangerously liberal or nearly powerless. It identifies a recommended core of five tests—McCullagh, Osius–Rojek, le Cessie–van Houwelingen, Stute–Zhu, and GiViTI—that best balance Type I error and power. A real-data example with omitted interactions shows that even this core can miss structured misfit, so the paper argues that a panel of tests plus a visual calibration (reliability) curve, not any single p-value, should be the routine check.

Core claim

The central claim is that under fully sparse data (J ≈ n covariate patterns), the usual textbook tests are unreliable, but a compact set of five procedures—the standardized-Pearson tests of McCullagh and Osius–Rojek, the kernel-smoothing test of le Cessie–van Houwelingen, the CUSUM bootstrap test of Stute–Zhu, and the GiViTI polynomial calibration test—delivers empirical Type I error near the nominal 5% across a wide range of covariate distributions and sample sizes while showing higher power than Hosmer–Lemeshow against omitted quadratic and interaction terms. The paper also claims that no single test is sufficient: in the low-birth-weight example, a misspecified model with omitted interact

What carries the argument

The central object is the benchmark itself, organized through a six-family taxonomy of goodness-of-fit and calibration algorithms: partition/grouping tests, standardized-Pearson tests, score/link tests, smoothing tests, calibration tests, and bootstrap tests. The comparison runs under a standard simulation design with five covariate distributions, two misspecifications at two severities, five sample sizes, and 10,000 replications per scenario, with every test applied to the same simulated dataset so all comparisons are paired. The key mechanism shared by the recommended tests is recovering a valid null distribution under sparsity: Osius–Rojek and McCullagh standardize the Pearson statistic b

Load-bearing premise

The whole comparison rests on the authors' own implementations of the roughly twenty-five tests being faithful to the published methods, especially the McCullagh variance formula and the GiViTI internal null distribution; if those implementations are wrong, every size and power estimate—and the apparent advantage of the recommended core—could shift.

What would settle it

Run the recommended five tests on a published example with a known correct logistic fit using an independent implementation (for instance, a mainstream statistics package), and check whether the p-values match those reported here. If the McCullagh or GiViTI p-values differ systematically from the published methods, the benchmark's rankings are not reliable. Alternatively, rerun the simulation with a different implementation and see whether the five-test core still beats Hosmer–Lemeshow on sparse data.

Watch this falsifier. Get emailed when new claim-graph text bears on it.

If this is right

  • Practitioners should stop relying on a single Hosmer–Lemeshow p-value when checking sparse logistic fits; the recommended five-test panel matches or beats its size control while being consistently more powerful.
  • Raw Pearson, deviance, the Hosmer–Lemeshow F-test, and the bootstrap Hosmer test should not be used on sparse continuous data because they reject correctly specified models far too often.
  • Over-conservative tests like Spiegelhalter and eHL, and essentially powerless tests like Farrington and the unreliability index, are unsafe as standalone checks.
  • A calibration (reliability) diagram with a nonparametric curve can expose structured misfit that omnibus p-values miss, and should accompany any panel of tests.
  • Even the recommended core can fail on real data, so robust assessment requires triangulating several diagnostics rather than trusting any single test.

Where Pith is reading between the lines

These are editorial extensions of the paper, not claims the author makes directly.

  • If the benchmark is right, the same ranking may not hold in high-dimensional or penalized logistic models, since the paper explicitly leaves link-function misspecification, clustered data, and penalized fits for future work; a natural extension is to test the recommended core under ridge or lasso fits.
  • The finding that grouped-data tests caught the omitted interaction in the low-birth-weight example suggests a hybrid strategy: in near-sparse data with a few repeated covariate patterns, complementing the sparse-data core with a grouped statistic may be more sensitive than any fully sparse test alone.
  • The GiViTI internal null distribution and the McCullagh variance formula used in the paper are nonstandard; an independent implementation check against published numeric examples would directly test whether the benchmark's ranking is an artifact of the software.
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Editorial analysis

A structured set of objections, weighed in public.

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

Referee Report

4 major / 5 minor

Summary. This paper provides a taxonomy and an empirical comparison of roughly 25 goodness-of-fit and calibration tests for binary logistic regression in the sparse-data regime (continuous covariates, J≈n). The authors implement the tests in a new R package, ebrahim.gof, and run a large simulation study (10,000 replications; five covariate distributions for Type I error; two misspecification types at slight and pronounced severity for power; n=200–5000). Based on the simulated size and power, they recommend a core of five tests—McCullagh, Osius–Rojek, le Cessie–van Houwelingen, Stute–Zhu, and GiViTI—as more powerful than Hosmer–Lemeshow while maintaining size. A low-birth-weight example illustrates that a single p-value can miss omitted interactions and motivates pairing tests with a calibration curve.

Significance. If the benchmark is trustworthy, the practical payoff is high: it gives applied users an evidence-based alternative to the default Hosmer–Lemeshow test and a compact panel to report. The study is carefully executed at the simulation level: seeds, 10,000 replications, paired comparisons, Monte-Carlo standard errors, an α=0.01 robustness check, and an archived code repository. The taxonomy is useful even if the rankings were to shift. The main risk is that all test implementations come from the authors' own package, with no independent verification of the two most nonstandard algorithms (McCullagh and GiViTI). The paper's central recommendation therefore cannot be accepted on the current evidence without implementation-level validation.

major comments (4)
  1. [Appendix A, Algorithm 3, Step 6] The conditional variance formula Var(X^2|βhat) = (1-p*/n)(2Σ(m_i-1)/m_i + RSS_u) reduces to (1-p*/n)RSS_u for pure binary data. This is not the textbook form of McCullagh (1985) and is load-bearing: it determines the standardization of every McCullagh p-value and therefore the test's size and power in all tables. The paper offers no check against the original derivation, published numerical examples, or an independent implementation. Please add verification (e.g., reproduce known conditional moments in a simple design or compare with a published implementation) before the core recommendation can be accepted.
  2. [Appendix A, Algorithm 6, Step 20] The internal-validation null CDF F_m (Nattino et al. 2016, Eq. 10) is not a standard chi-square and is not implemented or documented in the paper. The GiViTI p-value, and hence its inclusion in the core, depends on the numerical evaluation of F_m. Without stating how F_m is computed (quadrature, simulation, closed form) and validating it (e.g., against givitiR or Nattino's tables), the reported Type I error and power for GiViTI cannot be independently reproduced.
  3. [Sections 3.3 and 4.4] Power is simulated only for x~U(-3,3), while the Type I study spans five covariate distributions. The core-selection rule in Section 4.4 requires 'ranks among the strongest performers in the slight-misspecification regimes', but those rankings come from a single covariate distribution. Given that size behavior changes substantially across the distributions in Figure 1, power rankings may also change under skewed/sparse covariates. Either run power scenarios for at least one additional covariate distribution (e.g., χ²(4) or U(-6,6)) or restrict the recommendation to the U(-3,3) misspecification settings. This is load-bearing for the general claim in the abstract that the core 'delivers the best balance' across sparse data.
  4. [Section 4.4] The recommended core is selected after inspecting the same simulation results it is then recommended from, with no confirmatory split or pre-specified selection rule. The qualitative 'simple reading' criterion is not fully operationalized (e.g., exact size thresholds and power ranks are not given), and the apparent advantage of the core could partly reflect selection on the same random draws. A validation round on held-out scenarios or a fully specified decision rule with sensitivity analysis would strengthen the central recommendation, especially because the implementations are from a single new package.
minor comments (5)
  1. [Abstract / Section 3] The abstract says 'four misspecification scenarios'; this should be clarified as two misspecification types, each at two severities, to avoid seeming broader than the design.
  2. [Section 3.1] The phrase 'the default bandwidth holding ≈√n points for le Cessie' is vague. Specify the kernel, the bandwidth rule, and whether it is the implementation in ebrahim.gof or the original paper's rule.
  3. [Algorithm 2, Step 9] For ungrouped data A=0 and the denominator becomes sqrt(RSS). If RSS is zero or near zero (e.g., intercept-only or saturated designs), the Osius–Rojek statistic is unstable. Please discuss or exclude such degenerate cases.
  4. [Algorithm 5, Step 12] The bootstrap p-value uses the indicator 1{T* ≥ T_obs}; please state the tie-handling convention and report the Monte Carlo error associated with B=200 bootstrap replications per fit.
  5. [Table 4] The 'PR+GAM' p-value of 0.069 is described as borderline; consider stating explicitly that it is not significant at the 5% level, to avoid ambiguity in the narrative.

Circularity Check

0 steps flagged

No significant circularity: the benchmark is an empirical evaluation against simulated ground truth; implementation-fidelity concerns are correctness risks, not circular steps.

full rationale

This paper is an empirical simulation benchmark, not a derivation from first principles. The recommended core is a summary of simulated Type I error and power under the published Hosmer et al. (1997) framework, with data generated from known correct and misspecified models. The tests are external published algorithms re-implemented in the authors' package ebrahim.gof; no test parameter is fitted to the benchmark outcomes and no fitted value is renamed as a prediction. The acknowledged dependence on the authors' own implementation (notably McCullagh's conditional variance and GiViTI's internal null CDF) is a reproducibility and fidelity risk, but it is not circularity: the package is a re-implementation of prior external methods, and the simulations have independent ground truth. There are no self-citations used as load-bearing evidence, no imported uniqueness theorems, and no ansatz smuggled in via self-citation. The taxonomy is explicitly non-canonical and adopted for convenience. Implementation bugs would affect the conclusions, but that is a correctness concern, not a circular derivation.

Axiom & Free-Parameter Ledger

5 free parameters · 5 axioms · 0 invented entities

The central ranking depends on hand-chosen simulation severities and on faithful implementation of ~25 published tests. No new entities are postulated; the only new artifact is the R package, which is a re-implementation.

free parameters (5)
  • Quadratic severity anchor Q = 0.01 (slight), 0.4 (pronounced)
    Hand-chosen anchor probabilities that set the true coefficients in the omitted-quadratic power scenario (Section 3.3). The test ranking could differ at other severities.
  • Interaction severity anchor I = 0.1 (slight), 0.7 (pronounced)
    Hand-chosen anchor probability difference setting the interaction coefficient (Section 3.3). Power rankings may be sensitive to this choice.
  • GiViTI forward-selection threshold q = 0.95
    Conventional default for the GiViTI calibration belt (Algorithm 6). Inclusion of GiViTI in the core may depend on this setting.
  • le Cessie bandwidth = ≈ sqrt(n) points
    Standard default bandwidth for the kernel smoother (Algorithm 4). Localized power could change with bandwidth.
  • BAGofT resamples nsim = 100
    Number of resamples for the BAGofT test; affects the resolution of its empirical p-value.
axioms (5)
  • domain assumption The Hosmer et al. (1997) simulation framework's data-generating scenarios are representative of realistic sparse logistic regression settings.
    The entire benchmark's generalizability rests on this; only five Type I covariate structures and two power-generating structures are used (Section 3).
  • standard math The asymptotic reference distributions used by each test (e.g., chi-square with G−2 df for HL, standard normal for Osius–Rojek and McCullagh) are valid under the simulated null.
    These distributions are the basis for all reported p-values; violations under sparsity are the very phenomenon being studied.
  • domain assumption The implementation of each test in ebrahim.gof is faithful to its published definition.
    A bug in any implementation (e.g., McCullagh's variance formula, GiViTI's internal null CDF) would change every size and power estimate. No independent verification is provided.
  • standard math The model-based bootstrap for Stute–Zhu, which resamples responses from the fitted model, is valid under H0.
    This is the standard parametric bootstrap for the CUSUM test (Algorithm 5, Part 2).
  • domain assumption The anchor-probability method of setting coefficients controls severity without inducing pathological separation.
    Coefficients are solved from fixed anchor probabilities (Section 3.3); this assumes the resulting data are representative of real misspecifications.

reviewed 2026-08-01 · how reviews work

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Cite this review

Pith. "Pith review of Benchmarking Goodness-of-Fit and Calibration Algorithms for Logistic Regression Classifiers: A Large-Scale Simulation Study under Sparse Data." pith.science (2026). https://pith.science/paper/CSKU2NYW

@misc{pith2026260716344,
  author       = {Pith},
  title        = {Pith review of: Benchmarking Goodness-of-Fit and Calibration Algorithms for Logistic Regression Classifiers: A Large-Scale Simulation Study under Sparse Data},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/CSKU2NYW}},
  note         = {Machine review of arXiv:2607.16344}
}
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read the original abstract

Binary logistic regression is among the most widely used classification algorithms, yet a classifier is only trustworthy if its predicted probabilities are well calibrated. The classical checks -- the Pearson chi-square and deviance statistics -- break down precisely in the modern setting where predictors are continuous and the data are sparse (one covariate pattern per observation). Four decades of research have produced dozens of alternative goodness-of-fit and calibration algorithms, yet practitioners still default to the Hosmer-Lemeshow test because it ships with their software. This paper provides a unified taxonomy and a large-scale, reproducible simulation benchmark; more than twenty tests are implemented in the open-source R package ebrahim.gof. We evaluate them across five covariate distributions and four misspecification scenarios, with 10,000 replications each, measuring both Type I error and power. Several classical tests prove liberal, rejecting correct models far too often, while others have little power. A compact core -- McCullagh, Osius-Rojek, le Cessie-van Houwelingen, Stute-Zhu, and the GiViTI calibration test -- delivers the best balance of correct size and high power, and is consistently more powerful than the ubiquitous Hosmer-Lemeshow test. A low-birth-weight application reinforces the point: a model with omitted interactions slips past nearly every test, exposed only by pairing sensitive tests with a calibration (reliability) curve. We translate these findings into practical, evidence-based guidance for assessing logistic regression fit.

Figures

Figures reproduced from arXiv: 2607.16344 by Ahmed El-Kotory, Ebrahim Khaled Ebrahim.

Figure 1
Figure 1. Figure 1: Type I error (empirical rejection rate at [PITH_FULL_IMAGE:figures/full_fig_p009_1.png] view at source ↗
Figure 2
Figure 2. Figure 2: Power (empirical rejection rate under misspecified models) by test and sample size, for [PITH_FULL_IMAGE:figures/full_fig_p011_2.png] view at source ↗
Figure 3
Figure 3. Figure 3: Excluded algorithms. Top row: Type I error (the classical Pearson, deviance, HL [PITH_FULL_IMAGE:figures/full_fig_p012_3.png] view at source ↗
Figure 4
Figure 4. Figure 4: Reliability diagram for the low-birth-weight model (fitted without interactions). The [PITH_FULL_IMAGE:figures/full_fig_p014_4.png] view at source ↗

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This paper was first reviewed by deepseek-v4-flash on August 1, 2026.