The WDBC repository describes nuclear feature extraction and a separating-plane construction using a small-feature exhaustive search [1]. The present wrapper uses an SVM [3] to score candidate masks. Its results should be compared with earlier methods only under compatible datasets, partitions, preprocessing and tuning protocols; published accuracy numbers from different protocols are not a common leaderboard. Nature-inspired search provides a range of update rules for wrapper optimization [2, 4–9]. Their performance is empirical and problem-dependent. This comparison examines ten alternatives to MPA, but does not establish that other medical feature selectors or simpler deterministic baselines have been exhausted.

Filter methods score variables independently of a chosen learner, wrappers evaluate subsets through a fitted prediction model, and embedded methods perform selection within model fitting. A wrapper can capture learner-specific interactions, but repeated scoring can overfit its validation criterion. Final predictive performance must therefore be assessed on data that played no role in selecting the mask or configuring the learner.

The objective studied here is a weighted scalarization of classification error and subset cardinality, rather than a Pareto optimization procedure. Overall accuracy weights errors according to class frequency and does not encode a larger false-negative cost. The coefficient 0.9 is a design choice about accuracy and feature count, not an empirically elicited clinical risk preference.

The canonical MPA implementation schedules a Brownian phase, a mixed Brownian-Lévy phase and a late Lévy phase, with elite, memory and environmental perturbation operations [2]. The interpretation of these operations as exploration or exploitation is conditional on the landscape and parameter settings. A best-fitness trace alone cannot identify which component causes an observed gain.

A binary wrapper also needs a precise transfer rule, continuous bounds, clipping convention and empty-mask policy. The reported use of a hyperbolic tangent does not determine these choices. A nonnegative V-shaped probability may use |tanh(z)|, but whether it flips an existing bit or assigns a new bit changes the algorithm. The experimental implementation must determine which rule was actually evaluated.

The comparison includes GA [10], PSO [11], DE [12], ABC [13], GWO [4], WOA [5], HHO [6], AO [7], SMA [8] and SSA [9]. This is a specified comparator set rather than the full contemporary metaheuristic landscape. Each continuous-to-binary adaptation and its objective-call budget must be documented consistently.

WDBC consists of 569 records with thirty morphology features and two classes, 357 benign and 212 malignant [2]. The features describe nuclei from digitized fine-needle aspirates. These are correlated image-derived descriptors, not independently validated molecular biomarkers.

Table 1 records the dataset properties. There are no missing values in the distributed dataset [1]. The malignant proportion is approximately 37.3%, making sensitivity, specificity and the aggregation of overall accuracy important when interpreting the results.

The reported procedure uses a 70% training and 30% stratified test split and five-fold cross-validation within training. Standardization is estimated from the training partition rather than the test set. For cross-validation fitness, scaling must additionally be fitted inside each training fold to prevent validation-fold information from entering the scaler. The source description does not resolve whether that nesting was implemented, whether the split was fixed across runs, or how SVM C and kernel gamma were chosen. The test set must remain outside mask selection and all tuning.

A feature mask x is a binary vector of length d = 30, with s selected variables. The minimized scalar objective shown below uses training-only cross-validation accuracy as a fraction in [0,1], combining its complement with normalized mask cardinality. The treatment of an empty mask must be specified because an SVM cannot be fitted without features. No asymmetric clinical error cost or global-optimality guarantee is encoded by this formula.

f(x) = α(1 − AccCV(x)) + (1 − α) , α = 0.9.

The wrapper represents a candidate by a continuous search state and a binary feature mask. The mask is evaluated by an SVM using training-partition cross-validation, and the scalar fitness guides the MPA search. The reported phase schedule follows the Brownian, mixed and Lévy phases of MPA [2]. Fig. 1 shows the intended workflow. The evaluated implementation must specify memory replacement, environmental perturbations, phase boundaries and the binary transfer convention; these cannot be reconstructed uniquely from the diagram.

At termination the procedure returns the best mask found under its computational budget and a classifier fitted without using the test labels. The returned mask is a heuristic solution, not a proven optimum. An interchangeable optimizer interface facilitates comparison only when its data access, scoring and evaluation budgets are controlled.

The recorded GA settings are tournament selection, single-point crossover probability 0.8 and bit-flip mutation probability 0.05. PSO uses inertia decreasing from 0.9 to 0.4 and cognitive and social coefficients 2.0. DE uses a rand-to-best mutation strategy, factor 0.5 and crossover probability 0.9. The ABC description specifies a 100-trial abandonment limit but does not uniquely define employed, onlooker and scout allocation. Other optimizers are described as following their source publications [4–8]. Population size 20 and 100 iterations are shared. Applying a transfer function to methods already operating on bits, and additional objective calls in multi-stage updates, must be distinguished in the implementation record.

Transfer function tanh (binary) Binary update convention unresolved Weighting alpha 0.9 Reported accuracy-cardinality preference Search dimension d 30 WDBC feature count

Table 2 records the common design settings. The RBF SVM configuration and its training-only parameter selection must be fixed across optimizers. Equal population size and iterations do not imply an equal number of fitness evaluations, so the table does not by itself prove budget fairness. Thirty stochastic runs describe optimizer variability on the chosen data; they are not thirty independent clinical cohorts.

Let E be the actual number of mask evaluations, K the number of cross-validation folds and C(n,s) the per-fold fitting and scoring cost for n training observations and s selected features. The principal wrapper cost is approximately E·K·C(n,s), plus search-update and preprocessing costs. Kernel construction contributes O(n²s), while solver cost and memory depend on the SVM implementation and data. Fewer features may reduce kernel construction cost, but no wall-clock advantage follows without measured runtimes, hardware details and objective-call counts.

Performance is summarized by accuracy, F1, ROC AUC, sensitivity, specificity and selected-feature count. Malignant is the positive class in the reported encoding. For a common fixed test population, accuracy satisfies Acc = π·Sensitivity + (1−π)·Specificity, where π is malignant prevalence. Table 3 requires reconciliation with this identity or an explicit explanation of differing evaluation populations and averaging. The reported one-sided Wilcoxon comparisons use per-run accuracy; valid pairing must share the experimental split and randomization unit [14]. The nominal p-values in Table 5 do not independently establish corrected significance.

The protocol reports thirty runs of each of eleven methods, totaling 330 optimization runs, with masks, training cross-validation scores, test metrics and convergence traces. Those run-level outputs, code, split indices, classifier parameters and environment versions are required to audit the recorded summaries. The reported Python, scikit-learn and SciPy implementation has no supplied versioned release or execution artifact, so exact numerical reproduction is not established by the present description.

In Table 3, MPA has the largest reported mean accuracy, 98.49%, 0.29 percentage points above HHO and 1.12 above the all-feature baseline. Its reported sensitivity is 98.56%. The accuracy standard deviation is 0.23 percentage points, rather than a variance of 0.23%; GA has the largest listed standard deviation, 0.90, followed by PSO at 0.78. These summaries do not prove generalization or stability outside the recorded runs, and their joint confusion-matrix consistency must be resolved.

The recorded accuracy ordering places MPA, HHO and GWO above 98.1%, with a 0.32-point span. SMA, WOA, DE and AO form an intermediate group. ABC and SSA exceed the all-feature baseline, whereas GA at 97.35% and PSO at 97.22% are below its 97.37%. Thus feature selection does not improve the listed mean accuracy for every optimizer. No mechanism or clinical advantage follows from this ordering alone.

Table 4 reports the feature-count means and standard deviations. MPA selects 11.13 variables on average, corresponding to 100(1 − 11.13/30) = 62.9% reduction. HHO and GWO retain means 12.37 and 13.33. PSO and GA retain 18.40 and 17.97. This describes mask size; measuring fewer correlated summaries from the same image does not automatically reduce specimen collection or imaging cost.

The recorded mean accuracy and subset size both favor MPA within this comparator set. Its 62.9% count reduction exceeds PSO's 38.7% by 24.2 percentage points. This is a descriptive accuracy-cardinality comparison, not evidence of a universal frontier or a validated eleven-marker clinical panel. Fig. 2 visualizes the subset-count summaries.

These bars describe variability in count, not agreement in feature identity. Stability of a selected mask would require overlap or selection-frequency analyses and validation on resampled or external data.

Fig. 3 shows the reported median best-fitness trajectories. MPA decreases early and continues to improve within the recorded iteration budget, while some comparators plateau earlier. Best-fitness traces describe optimizer progress under the scalar objective; they cannot separate the effects of Brownian updates, Lévy steps, memory or binary repair without component ablations.

The recorded terminal objective values broadly follow the accuracy-cardinality ordering. A lower scalar fitness can reflect either lower cross-validation error or fewer variables, and must not be interpreted as test accuracy alone. Comparing traces by iterations also requires objective-call counts because one iteration can contain different amounts of scoring work.

Table 5 retains ten reported one-sided Wilcoxon statistics and nominal p-values. The HHO comparison has p = 0.0057 and the GWO comparison p = 0.0010; eight comparisons are listed as p < 0.0001. Nine p-values are therefore at or below 0.001, rather than strictly below it. Paired run outputs and tie handling are needed to reproduce the tests.

Multiplicity changes the interpretation of nominal significance. A Bonferroni threshold for ten comparisons is 0.005, which the HHO value 0.0057 does not meet. Holm correction could retain all ten recorded comparisons if the reported nominal p-values and pairing are correct, but adjusted results have not been independently reconstructed from the runs. These tests concern optimizer randomness under the experimental data design, not clinical sampling uncertainty.

Fig. 4 displays the recorded accuracy distributions across runs. MPA has the highest central location and the smallest listed accuracy standard deviation. Overlap between distributions, shared test observations and unresolved metric aggregation limit interpretation; the plot does not establish a causal explanation of search behavior.

Fig. 5 displays the reported feature-selection frequencies. Several mean and worst-value morphology descriptors are frequently retained, while many standard-error features are less frequent. A frequency pattern reflects the wrapper, correlated predictors and the data partition; it does not validate the biological role of a feature or show that all low-frequency features are uninformative.

The heatmap suggests a common predictive core across methods and differences in how broadly they retain variables. Interpreting sharper frequency differences as a Lévy-driven effect would require an ablation with the same evaluation budget. Identifying a clinically reliable mask additionally requires stability assessment and validation outside WDBC.

Fig. 6 summarizes the recorded metrics using normalized radar axes for MPA, HHO, GWO and SMA. Its apparent polygon areas depend on normalization, axis order and the chosen feature penalty. The tabulated values provide the quantitative comparison; radar area is not a statistical test, utility function or Pareto certificate.

Fig. 7 plots mean accuracy against mean subset size. MPA is the most favorable recorded point in this two-dimensional comparison. The all-feature baseline has the largest count, but exceeds GA and PSO in reported accuracy. This plot illustrates trade-offs among the measured means rather than proving that every feature selector improves generalization.

MPA's phased movement, memory replacement and environmental updates are plausible contributors to search performance [2]. The recorded convergence curves do not isolate their effects. Controlled ablations and matched objective-call budgets would be required to determine whether Lévy movement, memory or the binary encoding explains the observed ordering.

Memory is not unique to MPA: canonical PSO stores personal and global bests [11], and GA can use elitist retention [10]. The reported standard deviations, 0.23 for MPA and 0.78 for PSO, describe these configurations rather than an inherent stability ordering of their algorithm families. Wilcoxon tests compare output distributions and do not identify a memory mechanism.

Exploration and exploitation depend on both update rules and the evaluated landscape. Larger subsets or early plateaus do not diagnose an optimizer as excessively exploratory or exploitative. The recorded comparison is useful for this wrapper configuration, but a mechanistic interpretation needs controlled changes to the search components and budgets.

HHO and GWO have near-MPA reported accuracies with larger mean masks. HHO's rapid-dive operations can themselves use Lévy steps [6], so their absence cannot explain MPA's result. Compactness may matter in choosing an experimental configuration, but this comparison does not establish clinical superiority or a universally preferred optimizer.

Selected radius, perimeter, area, concavity and concave-point descriptors quantify nuclear morphology [1]. Their frequent selection is compatible with predictive use of size and contour information. Correlation among descriptors and the lack of external biological validation prevent treating the optimizer output as identification of independent disease mechanisms.

Lower selection frequency for standard-error variables does not establish that they lack diagnostic information. The wrapper can substitute correlated descriptors, and a selection pattern on one dataset may change under resampling, a different classifier or a different objective. Biological interpretation should therefore remain descriptive.

Comparisons with prior medical classifiers require equivalent data, splits, preprocessing, tuning and metrics. Accuracy figures reported under other protocols cannot establish a discriminative ceiling or a state-of-the-art ordering for the present wrapper. The contribution is the specified comparator experiment and its documented limits, rather than a cross-paper accuracy ranking.

The eleven-method suite is broader than a two-method comparison, but its coverage is finite. Formal tests add information only when run pairing and data dependence are explicit [14]. The unresolved confusion-matrix identity and implementation record are more important to validity than the number of competitors or nominally significant p-values.

This study uses a single retrospective benchmark and one wrapper learner. Training-only cross-validation, scaling nested inside folds, a documented untouched holdout and clear SVM parameter selection are needed to assess leakage. The reported accuracy, sensitivity and specificity require a common averaging convention and paired confusion matrices before performance conclusions can be considered validated.

The fixed population and iteration settings do not prove matched objective-call or tuning budgets. Run-level outputs are also needed to reproduce significance tests and quantify subset identity stability. No prospective cohort, clinical workflow cost, mechanism ablation or independent external validation is reported. These are substantive limits on publication and translation, rather than evidence that the recorded ranking must generalize.