Supervised machine learning in clinical settings is rarely limited by the availability of unlabeled patient records; it is limited by the expert time required to label them. Diagnosis codes, histology readings, and adjudicated outcomes are produced by scarce specialists, so the labeling budget of a typical clinical modeling project covers only a small fraction of the candidate cohort. Active learning addresses this bottleneck by letting the model choose which instances to label: starting from a small seed set, the learner scores the unlabeled pool, queries the most promising instances, and re-trains [1]. In the three decades since uncertainty sampling and Query-by-Committee (QbC) were introduced [2], [3], a large toolbox of acquisition heuristics has accumulated, but their behavior under the data pathologies that characterize clinical tabular data—class imbalance and label noise—remains patchily documented.

WDBC contains thirty morphology descriptors and binary diagnoses [4]. The stress regimes examine class subsampling and corrupted training annotations separately; they do not represent two independent cohorts or a simultaneous imbalance-plus-noise condition. Uniform corruption locations provide a controlled intervention but cannot represent every real annotation-error mechanism [1].

The original data contain 569 records, 212 malignant and 357 benign [4]. The imbalance condition retains 89 malignant records and all benign records, redrawing the subsample per seed; the ratio is approximately 1:4. The noise condition changes 39 of 398 training labels at uniformly selected positions fixed before querying, a realized rate 39/398 = 0.09799. Test labels remain clean. Five strategies and three learners are compared across the same initial labeling budgets.

The recorded Area-Under-Learning-Curve (AULC) summaries favor active acquisition across the reported cells. Logistic regression under noise increases from 0.9587 to 0.9837, with the retrospective mean threshold budget decreasing from 32.0 to 24.7. Nonnegative cell medians do not mean every individual run benefits. The study examines a paired simulation design; validating its numerical conclusions requires the original trajectories, acquisition logs, statistical analysis and versioned execution materials.

Uncertainty, margin and entropy scores for one binary probability vector are monotone functions of distance from probability one half [1], [2], [5]. With exactly the same fitted model, pool and tie convention, they therefore select identical ranked batches. This mathematical equivalence does not establish that separate stochastic fitting or implementation paths were identical.

QbC bases acquisition on disagreement among hypotheses [3], [6]. The tested variant is described as a five-member bagged committee of the selected learner, scored by normalized vote variance. This particular bootstrap and score choice is an implementation of the committee idea, rather than the theoretical selective-sampling construction analyzed in [6]. Historical pool-based text classification combined committee acquisition with expectation maximization [7].

Density- and hierarchy-based acquisition offers a complementary emphasis on input coverage. Dasgupta and Hsu analyze hierarchical sampling under their specified model [8]. Such results motivate considering representation and class prevalence, but do not imply that uncertain boundary regions are always majority dominated. Noisy-oracle behavior is also sensitive to the acquisition rule and error mechanism [1].

The learners are regularized logistic regression, random forest [9] and histogram gradient boosting, drawn from scikit-learn [10]. The classical gradient-boosting source [11] describes the methodological family, while the concrete histogram estimator has library-specific implementation and defaults. The comparison holds these configurations fixed; it does not rank all members of their model families.

The study asks how acquisition rules interact with learner choice and two separately constructed stress regimes. It also records cell-level and per-seed downside outcomes. It does not provide a general bound on active-learning risk or establish that previous comparisons were uniformly clean, balanced or anecdotal. The research questions concern retrospective label efficiency and variation among the specified learners and regimes.

RQ1 asks how the recorded AULC and retrospective budgets to test AUC 0.95 differ from random sampling, and how frequently individual seeds show a deficit.

RQ2 asks whether the reported mean strategy ordering changes with learner and regime, including the approximate 1:4 imbalance condition.

Two directional hypotheses guide interpretation. H1 anticipates benefits from committee and margin sampling under imbalance; H2 anticipates degradation of uncertainty sampling relative to random under noise. No dated registration record is supplied, so these are stated hypotheses without a preregistration claim. Comparisons use the reported Holm-corrected paired AULC tests, with their direction retained regardless of the anticipated outcome.

The reported environment construction subsamples the imbalance condition before a stratified 30% test split, fixes any training-label corruption before querying, and draws the initial labeled set and pool from training only. StandardScaler is described as fitted to all training features once, including unlabeled pool features, and applied across rounds. This is a transductive use of unlabeled training covariates rather than test leakage or labeled-only preprocessing. Code assertions and split indices are needed to verify that test rows and labels did not influence fitting, querying, configuration selection or stopping.

The recorded design contains 90 seed-regime environments, each running five strategies and three learners from a common initial state. Fourteen evaluated budgets imply 90×5×3×14 =18,900 evaluation fits. Thirteen QbC rounds with five members and three learners imply 90×3×13×5 =17,550 committee fits. The source reports base seed 42, PCG64 seed sequences [42,seed,regimeindex], minimum observed minority count 4, zero split-assertion failures and mean corruption rate 0.0980. These execution diagnostics are reported rather than independently reproduced.

The execution record reports 324s on a workstation CPU with two workers, an environment phase 322s and mean 7.16s per environment, with figure generation 1.4s. It lists Python 3.12.14, NumPy 2.1.3 [14], SciPy 1.14.1 [15], scikit-learn 1.5.2 [10], statsmodels 0.14.5 [16] and Matplotlib 3.9.2 [17]. Hardware details, wall-time accounting and a versioned runnable artifact are required before those performance and reproduction claims can be verified.

Regime: Label noise 10% 39 of 398 train labels flipped (uniform, fixed per seed before querying; test labels clean); realized rate 0.0980; derived variant.

Split Stratified 30% test, drawn and frozen before any querying; pool = train-split rows only.

Initial labeled set 20 stratified rows (≥ 3 per class; minimum observed minority count 4), shared by all strategies (paired design).

Query protocol Batch mode, top-10 scoring instances per round; budgets 20– 150 step 10 (14 points).

Strategies Random; uncertainty; margin; entropy; QbC (5-member bagging committee, vote disagreement 4v(1−v)).

Learners LogisticRegression(max_iter=1000) on standardized features; RandomForest(n_estimators=30); HistGradientBoosting(max_iter=50); model random_state = 42 fixed.

Replications 30 seeds; base seed 42 (PCG64 sequence [42, seed, regime index]).

Metrics Test AUC per budget; AULC (normalized trapezoidal area over budgets 20–150); labels to AUC 0.95 (interpolated, censored at 150).

Statistics Paired Wilcoxon vs random: family A (AULC; 36 tests) and family B (learner-averaged AUC at budgets 50/100/150; 36 tests), each Holm-corrected; two-way ANOVA with partial η²; bootstrap 95% CIs (2,000 resamples).

The two stress regimes are derived transformations of the real WDBC data, documented in Section 4.4.

Table 4 retains Family A statistics:36 reported Holm-significant comparisons, largest adjusted p0.0039 and smallest 6.7×10⁻⁸, with rank-biserial range 0.65-1.00. FamilyB is reported as 36 significant comparisons, largest adjusted p0.0035 and rank-biserial range 0.60-1.00. The noise/budget 100 examples give median AUC deltas 0.0155 for uncertainty and 0.0160 for QbC, W 0 and adjusted p 6.7×10⁻⁸. Raw paired trajectories, zero handling, sidedness and the correction code are required to validate these recorded inferential summaries.

All tests favor the active strategy (positive median deltas; backfire analysis in Section 6.6). LR = logistic regression, RF = random forest, GB = gradient boosting.

The recorded ANOVA summary gives regime F(2,435)=53.60 with partialη²0.198, strategy F(4,435)=18.23 with partialη²0.144, and interaction F(8,435)=3.76 with partialη²0.065. These effect sizes agree with F times effect degrees of freedom divided by that quantity plus 435; they are partial associations, not percentages of total variance causally explained. A 450-observation design matches one learner across 30 seeds, three regimes and five strategies; pooling all learners would instead contain 1,350 observations unless an aggregation is specified. The reported collapsed-strategy summary F(2,261)=28.83 is similarly conditional on its unit and model. Original per-seed outputs and analysis code must resolve the model labeling and repeated-measures inference. Reported noise intervals are[0.9803,0.9869] for logistic-regression uncertainty and[0.9513,0.9655] for random. The mean ordering is compatible with H1 and opposite to H2, but no preregistration or causal interpretation is established.

The recorded original-regime logistic-regression baseline is near the upper end of the AUC scale, so remaining absolute improvements are small. Random sampling reaches reported AUC 0.987 at 30 labels, while several cells have AULC gains only in the thousandths. Some of these cells also have adverse individual seeds. This co-occurrence is descriptive: the study does not identify a causal relationship between the ceiling, variance of paired differences and the probability of underperforming random.

The largest recorded strategy premium occurs under the fixed-count noise condition, particularly for logistic regression. A plausible interpretation is that acquisition can provide more informative labeled examples for that learner. It is not established that adaptively selected and random batches experience the same conditional corruption rate: although locations were drawn uniformly before querying, past corrupted labels influence the evolving model and its future selections. Query-level corruption counts and controlled alternatives are needed to identify the mechanism.

Under imbalance, QbC has the largest reported mean AULC for each learner. This ordering does not establish that it preferentially acquires minority examples or is clinically the safest default. Under the studied noise process uncertainty outperforms random in the reported summaries, but this cannot be generalized to difficulty-correlated, class-conditional or adversarial annotation error [1].

The small-sample boosting floor and saturated threshold medians limit interpretation. A common initial floor affects subsequent query histories as well as the integral. The interpolated test threshold is retrospective and must not be used to choose a deployed stopping budget without independent validation. These facts matter when comparing learners as well as strategies.

The recorded summaries favor active acquisition over random at the cell level, with the largest logistic-regression gain under fixed-count noise. Individual seeds can nevertheless perform worse than random, and QbC does not dominate every noisy-regime comparison. The results concern the supplied single-dataset configurations and require original execution evidence to validate AULC, exact score-equivalence handling and inferential units. Extending the study to external cohorts, simultaneous stress regimes and realistic annotation mechanisms would be necessary before using it to select clinical labeling policies.

The study uses the public WDBC dataset [4] and derived class-subsampling and label-corruption conditions. No new primary data collection is described.

The computational protocol describes no patient contact or new human-participant intervention. Institutional requirements and any secondary-data approval statement must be confirmed by the author.

The source declares no funding and no competing interests. The author must confirm these declarations before publication.

The recorded seed scheme is documented in Section 11. Availability and numerical reproducibility of scripts, results and figures require an accessible versioned release.

The source declares AI assistance in text and code preparation. The author must identify the tools and tasks and confirm the independent validation of the scientific content; no execution or verification of the reported experiments follows from the disclosure itself.

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