International Journal of Artificial Intelligence Engineering and Transformation

Optimizing Regularized Logistic Regression Pipelines on Cleaned Biomarker Datasets: A Leakage-Proof Benchmarking Protocol for Diagnostic and Prognostic Modeling

Stanley Nwakamma1, Serif Oyindamola Oyesiji2, Harouna Wendpanga Yann Christian Sankara3, Toussida Fatah Tanguy Minoungou4

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Version of record

This is an author-deposited copy. The version of record was originally published elsewhere: Originally published in International Journal of Artificial Intelligence Engineering and Transformation, Volume 7, Issue 2, 2026. DOI 10.54660/IJAIET.2026.7.2.64-72 . Original source: https://www.artificialinteljournal.com/archives/year-2026.vol-7.issue-2.

Abstract

Logistic regression remains the workhorse of biomarker-based diagnostic and prognostic modeling, and for principled reasons: it yields calibrated probabilities when fitted and validated correctly, its coefficients support biological and clinical interpretation, and its statistical behavior under limited events is thoroughly characterized. Yet the gap between the method's textbook properties and its published practice is wide and documented, with prediction research reviews finding pervasive deficiencies in validation, calibration assessment, sample size justification, and handling of missing data, deficiencies that persist even in high-stakes settings. The availability of cleaned, curated biomarker datasets removes the data-quality alibi and exposes the remaining variance for what it is: modeling protocol. This paper develops a research concept for a systematic optimization and benchmarking protocol for logistic regression pipelines on cleaned biomarker datasets. The protocol fixes a leakage-proof evaluation harness, nested resampling with all preprocessing inside the resampling loop and grouping that respects study and batch structure, and then treats the pipeline's design space as the experimental object: regularization family and strength, feature selection strategy including stability-based selection, treatment of continuous predictors, class imbalance handling, missing data strategy, rare-event corrections, and post-hoc calibration methods, each varied under prespecified contrasts. Performance is reported as a profile, discrimination with uncertainty, calibration curves and indices, and decision-analytic net benefit across clinically relevant thresholds, never as a single headline number, with optimism-corrected internal validation and temporal or cohort-external validation where data permit. Prespecified hypotheses target the conditions under which elastic net dominates unpenalized fitting, when stability selection changes selected panels, and how far calibration methods repair miscalibration without refitting. Reporting follows prediction-model standards throughout.

Keywords: Logistic regressionBiomarker-based diagnosticsPrognostic modelingPredictive modelingModel calibrationRegularization

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1. Introduction

The statistical case for logistic regression in biomarker modeling has never weakened. The model's foundations are classical (Cox, 1958; Hosmer et al., 2013) [39, 55], its regularized extensions address the correlated, wide feature sets that biomarker panels produce (Hoerl & Kennard, 1970; Tibshirani, 1996; Zou & Hastie, 2005) [54, 107, 118], efficient solvers make the whole regularization path routine (Friedman et al., 2010; Pedregosa et al., 2011) [48, 89], and the surrounding methodology, events-per-variable behavior, modern sample size criteria, rare-event bias correction, and validation strategy, is mature and prescriptive (Peduzzi et al., 1996; van Smeden et al., 2019; Riley et al., 2020; Firth, 1993; Harrell, 2015; Steyerberg, 2019) [90, 112, 96, 47, 51, 103]. When more flexible learners are compared fairly on clinical tabular problems, regularized regression remains a strong and frequently undominated baseline (Hastie et al., 2009) [52]. Applied biomarker research continues to instantiate the setting directly, as in recent population-scale studies associating composite metabolic indices with estimated cardiovascular risk through regression-based analysis (Amadi et al., 2025) [15]. The same index literature extends that pattern across outcomes and cohorts, relating the triglyceride-glucose index to reduced kidney function along the cardio-renal continuum (Amadi et al., 2026a) [13], pairing it with echocardiographic measurement for stratification in Sub-Saharan African populations (Okwah, 2022) [79], and situating it against opportunistic screening estimates of hypertension burden (Amadi et al., 2026b) [14]. Adjacent work supplies the predictor classes such pipelines ingest: circulating inflammatory biomarkers and gene-expression readouts (Okwah et al., 2026) [80], nutritional exposures paired with DNA markers in diabetic cohorts (Ike et al., 2025) [56], and the modifiable-risk context that determines case mix and confounding structure (Abah et al., 2025a; Abah et al., 2025b; David et al., 2025) [1, 2, 40]. These are precisely the datasets on which the modeling choices this paper isolates are made.

The practice, by systematic account, does not match the method. Reviews of clinical prediction research document weak validation design, absent calibration assessment, unjustified sample sizes, and ad hoc missing data handling as the norm rather than the exception (Bouwmeester et al., 2012) [34], a pattern that reappeared at scale in the pandemic-era model literature, where a living systematic review appraised hundreds of models and found nearly all at high risk of bias (Wynants et al., 2020) [116]. The biomarker field carries additional documented pathologies of its own: selection bias and overfitting in discovery (Ransohoff, 2004; Ransohoff, 2005) [94, 95], inflated early effect sizes (Ioannidis & Panagiotou, 2011; Ioannidis, 2005) [61, 60], and evaluation by measures that overstate clinical usefulness (Pepe et al., 2004) [92], all against staged evidentiary frameworks that specify what validation should look like (Pepe et al., 2001) [91]. The same tension surfaces in evidence synthesis, where phenotype-stratified pooling is adopted precisely because averaged effects conceal the subgroup structure a prediction model is supposed to represent (Yusuf et al., 2026) [117], and in outcome-level reviews of complex interventions whose heterogeneity mirrors the case-mix variation that transportability analysis must handle (Obi et al., 2025) [71]. Methodological work has likewise shown that the most damaging errors are procedural: feature selection performed outside cross-validation biases error estimates catastrophically (Ambroise & McLachlan, 2002; Simon et al., 2003) [16, 101], model selection inside a single resampling loop biases them again (Varma & Simon, 2006) [113], and leakage in its many forms is now recognized as a general reproducibility threat in learning-based science (Kapoor & Narayanan, 2023; Whalen et al., 2022) [63, 115]. Cleaned data sharpens the question. As curated biomarker resources and standardized preprocessing become available, the residual variance in reported performance is increasingly attributable to pipeline choices, regularization, selection, imputation, calibration, and validation design, rather than to raw data quality, and those choices are rarely varied systematically or reported completely (Collins et al., 2015; Moons et al., 2015) [38, 68]. Curation also has an upstream that the term conceals: the cleanliness of a biomarker table is manufactured by laboratory design, pre-analytical control, and diagnostic workflow standardization long before an analyst sees it (Ogbete et al., 2018; Ayinde et al., 2026; Asiedu, 2023) [73, 32, 24], and by the governance and interoperability architecture that determines whether a variable means the same thing across contributing sources (Ilodigwe & Adesemoye, 2021; Aneke et al., 2023) [57, 21]. This paper develops the research concept for doing exactly that: a benchmarking protocol that treats the logistic regression pipeline as the experimental object on cleaned biomarker datasets, with a leakage-proof harness, prespecified contrasts, and profile-based reporting. Section 2 reviews background; Section 3 defines the problem; Sections 4 through 7 specify the protocol, the harness, the design space, and the calibration and decision-analytic layer; Section 8 sets out the evaluation and benchmarking plan; Sections 9 and 10 treat anticipated contributions and limitations; Section 11 concludes.

2. Background and Related Work

Prediction-model methodology supplies the protocol's spine. Modeling-strategy texts consolidate the discipline, prespecification, appropriate handling of continuous predictors, shrinkage, and internal validation by resampling (Harrell, 2015; Steyerberg, 2019) [51, 103], with fractional polynomial and related approaches giving continuous predictors principled functional forms rather than data-driven categorization (Royston & Altman, 1994; Sauerbrei et al., 2007) [97, 100]. Validation methodology distinguishes apparent, internally validated, and externally validated performance, quantifies optimism via bootstrap and cross-validation procedures (Efron & Tibshirani, 1993; Steyerberg et al., 2001) [43, 104], and warns precisely where naive designs fail: selection outside the loop (Ambroise & McLachlan, 2002; Simon et al., 2003) [16, 101] and tuning without nesting (Varma & Simon, 2006) [113]. Sample size methodology has moved from events-per-variable heuristics (Peduzzi et al., 1996) [90] to criteria targeting shrinkage and calibration stability directly (van Smeden et al., 2019; Riley et al., 2020) [112, 96], with penalized likelihood correcting small-sample and separation pathologies (Firth, 1993) [47]. Reporting standards close the loop, specifying what a trustworthy model paper discloses (Collins et al., 2015; Moons et al., 2015) [38, 68]. Performance assessment methodology defines the protocol's outcome space. Discrimination is measured by the area under the receiver operating characteristic curve with appropriate uncertainty and paired comparison machinery (Hanley & McNeil, 1982; DeLong et al., 1988) [50, 42], but discrimination alone misleads under imbalance and near decision thresholds, motivating precision-recall analysis (Saito & Rehmsmeier, 2015; Davis & Goadrich, 2006) [99, 41] and balanced summaries (Chicco & Jurman, 2020) [37]. Calibration is the clinically decisive property and the habitually neglected one (Van Calster et al., 2019) [111], assessed by calibration curves, slope and intercept, and proper scores (Brier, 1950; Steyerberg et al., 2010) [35, 105], and repaired post hoc, where refitting is impossible, by parametric and non-parametric mapping methods whose behavior is characterized in the calibration literature (Platt, 1999; Niculescu-Mizil & Caruana, 2005; Guo et al., 2017) [93, 69, 49]. Decision-analytic evaluation translates both into clinical terms, net benefit across threshold probabilities (Vickers & Elkin, 2006) [114]. The auxiliary design space carries its own methodology: imbalance handling by

4. Protocol Overview

The protocol has four layers executed in fixed order. The readiness layer verifies that the cleaned dataset supports the intended experiment: outcome definition and event counts against modern sample size criteria [96, 112], missingness mapped by variable and mechanism plausibility [65], structural metadata sufficient for grouped partitioning, and a data dictionary frozen before any modeling, with variable definitions, units, assay provenance, and permissible ranges recorded under the data-integrity discipline that regulated life-science operations already impose [21, 57, 12]. The harness layer instantiates the leakage-proof evaluation machinery of Section 5 and registers the prespecified design space and hypotheses. The experimental layer executes the design space under the harness, producing per-configuration performance profiles with uncertainty. The reporting layer renders results under prediction-model standards, full specification of every configuration, optimism-corrected estimates, calibration graphics, and decision curves, with code and configuration versioned for exact reproduction [38, 68, 89], and with access to identifiable inputs handled under the privacy-preserving architectures such data demands [27, 8]. The protocol's products are twofold: for the dataset at hand, a defensible model choice with its evidence; for the field, an accumulating benchmark of which pipeline choices matter under which named conditions.

5. The Evaluation Harness

The harness is nested, grouped resampling with the pipeline inside. The outer loop estimates generalization performance; the inner loop performs all tuning, penalty strength and mixing, selection thresholds, imputation hyperparameters, so that no outer estimate is contaminated by its own selection, the nesting whose omission biases error estimates [113]. Grouping assigns whole studies, sites, or batches to folds, so outer estimates approximate transport across structure rather than interpolation within it [64, 62], the structural unit in practice being the laboratory or collection network whose design, catchment, and throughput differ systematically from its peers [18, 75]; where only one structural unit exists, temporal splitting substitutes as the honest alternative. Every data-dependent operation, imputation models, transformations, screening, selection, calibration mapping, is fitted on training partitions only and applied forward, the discipline whose violation in feature selection was shown to fabricate accuracy decades ago and still recurs [16, 101, 63]. Uncertainty and correction are built in rather than appended. Optimism-corrected estimates via bootstrap validation accompany cross-validated ones, following comparative evidence on internal validation efficiency [104, 43, 51], paired comparisons between configurations use resampled differences with appropriate tests for correlated performance measures [42], and multiple imputation is executed per training partition with pooled downstream estimation under the standard combining rules [98, 110, 102]. The harness emits, for every configuration, the full profile, discrimination with intervals, precision-recall behavior at prespecified operating points, calibration curve with slope, intercept, and proper score, and net benefit across the registered threshold range [50, 99, 105, 35, 114], plus stability outputs where selection is in play [67].

6. The Pipeline Design Space

The design space is prespecified as factors with registered levels. Estimation: unpenalized maximum likelihood as the reference, ridge, lasso, and elastic net across the mixing range [54, 107, 118, 48], and Firth-penalized likelihood where event counts or separation indicate it [47]. Selection: none, embedded selection via the lasso path, univariate screening with false discovery control as the deliberately included bad-practice comparator whose cost the benchmark quantifies [33, 106], and stability selection over subsamples with selection-frequency thresholds [67]. Continuous predictors: linear, fractional polynomial, and spline treatments, with categorization excluded on the methodology's settled advice except as a costed comparator [97, 100, 51]. Imbalance: unweighted likelihood, class weighting, and synthetic minority oversampling as a sensitivity arm given its known calibration distortions [53, 36], an arm that matters most in the rare-outcome regimes that dominate applied risk stratification and detection work [81, 26]. Missing data: complete-case as the costed comparator, single imputation, and chained-equations multiple imputation [110, 65]. Calibration: none beyond the fitted model, parametric mapping, and non-parametric mapping, each fitted within the harness [93, 69, 49].

Crossing all factors fully is neither feasible nor informative; the protocol registers a fractional design anchored on hypotheses. Contrasts of primary interest, stated as prespecified hypotheses in the registration: elastic net dominates unpenalized fitting on the profile whenever events per variable fall below modern adequacy thresholds, with the margin growing as dimensionality rises [112, 96, 118]; stability selection changes selected panels materially relative to single-pass lasso while costing little discrimination, and its selection frequencies predict cross-fold panel reproducibility [67]; univariate screening's optimism, the gap between its inner and outer estimates, exceeds that of embedded selection, reproducing the classic selection-bias result under modern conditions [16, 101]; post-hoc calibration repairs slope and intercept miscalibration from imbalance interventions but not the local distortions synthetic oversampling induces [36, 69, 111]; and multiple imputation's advantage over complete-case analysis on the profile grows with missingness rate and structure, per the imputation literature's predictions [102, 98].

7. Calibration and Decision-Analytic Layer

The protocol elevates calibration and clinical utility from afterthoughts to registered endpoints. Calibration assessment is graphical and quantitative per configuration, curves with confidence bands, slope and intercept against the ideal, and proper scoring [105, 35], on the position that a biomarker model's probabilities are its clinical interface and their trustworthiness is not implied by discrimination [111]. Post-hoc calibration methods are treated as pipeline components inside the harness, so their apparent repairs are validated out-of-fold like everything else [93, 69]. Decision-analytic evaluation registers the clinically relevant threshold range with justification, rule-in and rule-out uses named, and reports net benefit curves per configuration against treat-all and treat-none references [114], converting profile differences into the currency that adoption decisions actually spend, and exposing the configurations whose discrimination advantages evaporate at the thresholds that matter [92]. Thresholds are registered with the deployment context named, since a probability consumed by an early-detection service, an operational triage dashboard, or a clinician-facing decision support tool carries different rule-in and rule-out costs and different tolerance for false positives [7, 5, 59, 58]. Where the dataset supports it, temporal or leave-one-study-out external validation is registered as the confirmatory tier above internal estimates, in the staged-evidence spirit of the biomarker frameworks [91, 103].

8. Evaluation and Benchmarking Plan

The plan proceeds in three phases. Phase one is harness verification: the machinery is validated on semi-synthetic data, real biomarker covariance with simulated outcomes of known coefficient structure, confirming that the harness recovers known signal, that its outer estimates are unbiased under the null, and that the registered leakage traps, selection outside the loop, unpooled imputation, ungrouped folds, are detected when deliberately introduced, the positive controls that give later results their credibility [63, 113]. Phase two executes the registered design space across a curated collection of cleaned biomarker datasets spanning the named conditions, events per variable, dimensionality, imbalance, missingness, and structural depth, reporting per-dataset profiles and cross-dataset patterns for each prespecified contrast, with disconfirmations reported as findings. The collection is assembled to vary provenance deliberately, because datasets drawn from different laboratory networks and diagnostic programs differ in measurement protocol and referral pattern as much as in case mix [19, 76, 25]. Phase three consolidates the benchmark: configuration-condition performance maps, the empirical answer to which choices matter when; stability atlases for selection methods across datasets [67]; and a reporting package per dataset that satisfies the prediction-model checklist end to end [38, 68], released with code, configurations, and seeds for exact reproduction [89], with the benchmark functioning as a release gate rather than a leaderboard [70, 3]. Acceptance for the protocol itself is defined operationally: results reproducible from the release, hypotheses adjudicated with registered analyses, and no reported estimate whose provenance the harness cannot certify leakage-free.

9. Anticipated Contributions

Three contributions are anticipated. For practice, the configuration-condition maps give biomarker modelers evidence-based defaults, when penalization is obligatory, when stability selection earns its cost, which imbalance interventions to avoid for probability-consuming uses, replacing the folklore that reviews show currently governs these choices [34, 116]. For methodology, the protocol operationalizes the literature's scattered prescriptions, nesting, grouping, imputation-within-validation, profile reporting, into one executable harness whose positive controls make violations visible, a transferable instrument for any tabular clinical modeling, not only biomarkers [51, 103, 115]. Because the harness is agnostic to the substantive domain, the same instrument answers the analogous question wherever tabular classification under imbalance and drift is deployed at scale, from anomaly detection and fraud screening to demand and segmentation modeling [28, 108, 66, 31, 78]. For the evidence base, the accumulating benchmark across cleaned datasets creates the comparative record that individual model papers cannot: how much performance variation is pipeline rather than biology, and where the honest ceilings lie for regression-based biomarker prediction under stated conditions [61, 94].

10. Limitations

The concept's boundaries are explicit. Scope: the protocol characterizes logistic regression pipelines; flexible learners enter only as registered challengers on identical folds, and claims about their relative merit are limited to the datasets and conditions studied [52]. Data dependence: cleaned does not mean representative, and curation itself can distort case mix and missingness in ways that qualify transportability; the structural grouping mitigates within-collection optimism but cannot manufacture external validity, which only the registered external tiers provide [91, 95]. Where a collection is dominated by a small number of laboratory networks, its case mix inherits their catchments and referral patterns [18, 72], and equity in who is measured at all remains a property of the diagnostic system rather than of the model [19, 74]. Design coverage: the fractional design answers its registered contrasts, not all interactions, and configuration-condition maps interpolate at their peril outside studied ranges.

Computational cost is real, nested grouped resampling with multiple imputation multiplies fits, and the released harness's efficiency work is part of the deliverable rather than an afterthought [48].

Two further boundaries are governance rather than statistics. The protocol assumes lawful access to individual-level data under prevailing privacy regimes, and the harness's appetite for structural metadata can conflict with the de-identification and minimization constraints those regimes impose [27, 8, 45, 85, 86]. And the protocol governs estimation and evaluation, not clinical adoption: net benefit curves inform but do not constitute impact evidence, the staged frameworks' downstream tiers, impact studies in deployment, remain beyond its remit [114, 103], and the organizational questions that decide whether a validated model is used at all, institutional readiness, oversight and accountability structures, and the regulatory route by which a model-derived tool reaches practice, sit outside the harness entirely [7, 9, 10, 22, 46, 20].

11. Conclusion

This paper has developed a research concept for the systematic optimization of logistic regression pipelines on cleaned biomarker datasets: a leakage-proof, structure-respecting evaluation harness with positive controls; a registered design space spanning regularization, selection, continuous-predictor treatment, imbalance handling, missing data strategy, and calibration; profile-based outcomes joining discrimination, calibration, and decision-analytic net benefit; and prespecified hypotheses that convert the field's methodological prescriptions into testable contrasts on real data. The concept's premise is that with curated data in hand, the pipeline is the experiment, and that the biomarker literature's documented gap between method and practice closes not through exhortation but through instruments, harnesses that make correct evaluation the path of least resistance and benchmarks that make the cost of bad practice a measured quantity. Executed, the protocol yields defensible models per dataset, transferable machinery for the field, and an evidence base on which the oldest tool in clinical prediction can be used at the standard its own methodology has long specified.

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