The central methodological contribution is the combination of periodic fold-based operator probing with smoothed credit allocation. Its value must be assessed against the evaluations consumed by those probes, rather than by comparing an equal number of generations.

The formulation specifies the parent-level improvement being measured, the distinction between uniform mixing and entropy regularization, and a budget-aware algorithm skeleton. Constraint penalties and noisy or Pareto-aware variants are separated from the bound-constrained experiment because their feasibility and performance have not been established by its tables.

The theoretical contribution is a conditional probability-of-hitting argument for an elitist incumbent. It does not supply a universal finite-time optimization rate, an exponential-weights regret guarantee, or local stability of the random population dynamics. These stronger conclusions do not follow from the stated credit update or covariance bound.

The empirical contribution consists of the supplied per-function results, original figures and auxiliary summaries. The 25 displayed CEC 2017 functions provide descriptive comparisons. The reported supplementary CEC 2022 and BBOB campaigns, raw logs, tuning traces and uncertainty calculations are not available in the materials supporting this revision and remain evidence dependencies.

A verifiable release must identify the implementation, operator definitions, seed mapping, actual function-evaluation counts, configurations and statistical input arrays. The source archive identifier has not been established as an artifact for this study; reproducibility is therefore a release requirement rather than a completed finding.

The following sections position the mechanism, define its credits and budget accounting, establish the scope of the conditional theory, and interpret the supplied results with their unresolved statistical and provenance requirements.

Fialho et al. [1] study bandit-based adaptive operator selection, while Thierens [2] develops adaptive pursuit with explicit allocation probabilities. These precedents already address the interaction between reward attribution and continued exploration. AOP-KFP differs in its proposed use of periodic held-out-parent comparisons within an evolving population. It cannot claim that adaptive pursuit invariably loses all exploration, nor that folds drawn from one population have the interpretation of independent cross-validation datasets.

An algorithm portfolio allocates trials among mechanisms rather than selecting a single mechanism in advance. In this study, allocation is based on exponentially smoothed, contemporaneous probe rewards. It is useful to distinguish this local adaptation from cumulative exponential-weights updates and from bandit rules with proved regret guarantees. Automatic configuration tools such as sequential model-based optimization [8] and irace [9] address a related allocation problem at the level of complete algorithm configurations.

The differential-evolution family offers parameter adaptation and population-size control as alternatives to a fixed search strategy. L-SHADE uses linear population-size reduction, while NL-SHADE-RSP uses nonlinear reduction and rank-based selective pressure [10], [11]. jSO and EBOwithCMA are included as named comparator implementations. Their version identifiers and settings are necessary to interpret the comparison; the source names alone do not determine their executed behavior.

Covariance matrix adaptation changes a search distribution using information from selected candidates. A full covariance update has different arithmetic and state costs from a coordinatewise mutation, even when each produces the same number of objective evaluations. A single covariance step inside a portfolio is also not automatically equivalent to a complete CMA-ES implementation with its own adaptation state and restart policy.

Population-level improvement measurements provide local feedback about the current search state. They differ from a general landscape characterization or an independent validation study. COCO provides standardized benchmark definitions and analysis infrastructure [12]. Invoking that infrastructure does not establish that the supplementary BBOB experiment was executed or that its results are available for inspection.

CEC 2017 and CEC 2022 provide benchmark definitions and evaluation criteria [13], [14]. The source reports 25 selected CEC 2017 functions in its principal table and names CEC 2022 as a supplementary campaign. Interpretation requires the exact suite version, function mapping and excluded-case record. Later analyses of CEC rankings [15], [16] are relevant methodological context, not authorization to discard difficult test functions. The modified official CEC 2017 report removes F2, whereas the supplied selected table includes F02; the exact earlier or modified function implementation therefore requires identification.

Friedman and post-hoc comparisons treat problems as comparison blocks when that is the specified design [5], [6], [17]. Run-level tests answer a different question and must identify their paired observations. Effect sizes [4], [18], [19], [20] complement significance tests but require an explicit direction, scale and unit of aggregation. Bayesian comparisons provide alternative inferential frameworks; no Bayesian robustness analysis can be certified without the corresponding inputs and outputs.

The credit recurrence is an exponentially weighted moving average, ĉ_j(v)=λĉ_j(v−1)+(1−λ)ḡ_j(v), indexed by probe round v. Hedge instead multiplies a previous weight by an exponential of the current reward, equivalent to accumulating rewards in log weights. Smoothing with a fixed forgetting factor is a different operation. A Hedge regret theorem therefore cannot be transferred to AOP-KFP by identifying the two recurrences.

Hyperparameter optimization offers useful configuration tools and budget-aware evaluation practices [8], [9], [21–24]. Bergstra et al. [24] introduce sequential approaches to hyperparameter optimization; that paper does not establish the random-search-versus-grid-search claim previously attached to it. The present probing rule evaluates search operators on current parents rather than estimating a model configuration’s performance on independent training and validation datasets.

Let Ω=∏ᵢ[aᵢ,bᵢ] be a compact box and f:Ω→ℝ be measurable and bounded below. Compactness alone does not ensure that a measurable function attains its infimum. We define the target value by

f★ = inf {f(x): x∈Ω}; Aε = {x∈Ω: f(x)≤f★+ε}, ε>0. (2)

The main experiment assumes exact evaluation of a fixed objective. A minimizer x★ is used only when attainment is separately assumed. The conditional result in Section 5 concerns objective sublevel sets Aε and explicitly assumes a positive probability of reaching each such set. For arbitrary measurable objectives, a single isolated optimum of zero proposal probability may violate this condition.

At generation t, the population P_t contains N evaluated candidates. Operator state includes any covariance, velocity, archive or crossover information used by its members. The allocation probabilities are held fixed between probing rounds. A separate incumbent stores the lowest objective value observed at any evaluated point, including points generated during probing.

At a probing round v, freeze P_t and its cached objective values before forming k disjoint folds F₁,…,F_k. For operator j and fold ℓ, construct any operator-specific state from the complementary parents P_t\Fℓ. Hold that state fixed while generating repaired offspring y_jℓ(x) for the held-out parents x∈Fℓ. The trials measure immediate improvement relative to those same parents.

A training rollout of r generations on complementary parents should be included only if it was part of the executed implementation. If used, every newly evaluated rollout point must be charged to the run budget. It must not mutate the common snapshot before the other operators are assessed.

The held-out comparison uses one evaluated candidate per held-out parent and the parent’s cached objective, after the specified bound repair. This aligns the comparison across operators without treating the population folds as independent test datasets. The fold score is

g_jℓ = |Fℓ|⁻¹ Σ_{x∈Fℓ} max{0, f(x)−f(y_jℓ(x))}; ḡ_j = k⁻¹Σℓg_jℓ. (3)

With one trial per held-out parent, all operators together require KN new objective calls per probe. If each complementary set is additionally evolved for r generations, those rollouts require rK(k−1)N calls, giving KN[1+r(k−1)] calls per complete probe. Neither count contains a factor d: one evaluation of a d-dimensional candidate is one objective call. The source does not resolve which rollout implementation produced the tables, so the logged count is essential for an equal-budget comparison.

Operator allocation mixes a softmax distribution with uniform exploration:

s_j(v)=exp(ηĉ_j(v))/Σ_h exp(ηĉ_h(v)); π_j(v)=(1−μ)s_j(v)+μ/K. (4)

Here η≥0 is an inverse-temperature parameter, μ∈[0,1) is a uniform mixture weight, and λ∈[0,1) controls credit smoothing. At probe round v,

ĉ_j(v)=λĉ_j(v−1)+(1−λ)ḡ_j(v). (5)

Between probes, credits and probabilities remain unchanged. For μ>0, π_j≥μ/K regardless of the softmax scores. This is a probability-floor statement, not a guarantee of spatial diversity or of useful rewards from every selected operator.

Bounds are enforced by the specified clipping map. A proposed extension for inequalities g_i(x)≤0 uses the comparison score:

Φ(x,t)=f(x)+ρ(t)Σᵢmax{0,g_i(x)}². (6)

For the finite horizon T, ρ(t)=ρ₀(1+t/T)^1.2 rises from ρ₀ to ρ₀2^1.2. This is a bounded penalty schedule. It does not repair violated constraints or guarantee feasibility. A constrained implementation must report constraint definitions and tolerances and retain a separate best feasible incumbent if a feasible output is claimed.

Algorithm 1 gives a budget-aware specification that resolves population size and score placement. B denotes a hard limit on new objective calls, whereas t counts generations. The source implementation must be checked against this specification before its tables can be attributed to the corrected accounting.

Algorithm 1. AOP-KFP.

Input: objective f, box Ω, population size N, objective-call budget B, and K operators; k folds, probe interval τ_probe, inverse temperature η, decay λ, mixture μ.

Output: best evaluated incumbent; for a constrained extension, report feasibility separately.

1. Initialize exactly N points using the chosen Latin-hypercube/Sobol mixture; evaluate and charge all N calls. 2. Set ĉ_j=0 and π_j=1/K; retain the best evaluated point as the incumbent.

3. Set generation t=0 and objective-call counter b=N.

4. While b<B:

5. If a complete scheduled probe fits the remaining budget:

6. Freeze the evaluated population and partition it into k folds.

7. For each operator j:

8. For each fold ℓ:

9. Build state or run the specified complementary-parent rollout; charge every new call.

10. Generate and evaluate held-out offspring; compute Eq. (3) and update the incumbent.

11. End fold loop.

12. Update only operator j’s credit by Eq. (5).

13. End operator loop.

14. Compute the mixed probabilities by Eq. (4).

15. End probe block; do not execute a partial probe as a complete comparison.

16. Sample an operator and generate a budget-permitted offspring batch.

17. Repair bounds; evaluate each new point and charge its call.

18. Update the best evaluated incumbent, including feasible status if applicable.

19. For constraints, compare Φ scores at the same t; never add a penalty to coordinates.

20. Select N survivors under the stated rule; increment t.

21. End while loop when the objective-call budget is exhausted.

22. Return the stored incumbent and the actual number of evaluations.

The nine source operator labels are listed in Table 1. Their heterogeneous state requirements must be specified independently: A crossover label needs a donor-generation rule, a PSO move needs velocity and personal-best state, and a covariance step needs an adaptation update. The aggregate frequencies in Fig. 7 summarize usage but cannot substitute for these definitions.

CMA-ES CMA-ES step (one full update of the covariance matrix) Particle swarm PSO velocity update (with constriction factor) Mutation operators Cauchy mutation, Gaussian mutation, Binomial crossover

Exponential smoothing favors recent probe improvements and forgets older evidence. For η>0, the unmixed softmax solves an entropy-regularized allocation problem:

s = argmax_{p∈Δ} {Σ_j p_jĉ_j + H(p)/η}, H(p)=−Σ_jp_jlog p_j. (7)

The final probability vector is then the explicit mixture π=(1−μ)s+μ/K. It is not the optimizer obtained by minimizing −p·ĉ+μH(p), whose entropy sign would favor concentration. The floor and the entropy term have distinct parameters and roles.

Comparing Φ(x_q,t)<Φ(x_p,t) constitutes penalized selection at the current generation. A bounded quadratic penalty can prefer an infeasible point whose objective improvement outweighs its penalty. Constraint satisfaction requires direct checking, and monotonicity of Φ across changing penalty coefficients does not establish monotonicity of the original objective or a feasible limit.

Objective-call accounting and arithmetic complexity are separate. Let C_f denote the cost of one objective call. A generation producing N evaluated offspring costs NC_f plus the operator’s internal work. Probe cost is added according to the executed rollout specification. Coordinatewise mutation or differential-evolution generation typically uses O(Nd) vector work. Full covariance sampling and updates can require O(Nd²), with additional decompositions of order d³ at their scheduled frequency. Applying one covariance step does not make that work linear in d. A held-out-only probe adds KN/τ_probe calls per generation on average. A complete r-generation complementary-parent rollout adds KN[1+r(k−1)]/τ_probe calls. With K=9, k=5, r=2, τ_probe=5, the latter equals 16.2N extra calls per generation, in addition to N ordinary offspring calls. Credit updates and a numerically stabilized softmax require O(K) scalar work at a probe.

Training state, temporary offspring and operator-specific matrices must also be included in memory accounting. A hard budget B bounds total objective calls including initialization and probes. It does not imply equal elapsed time across operators or equivalence to a baseline run for the same number of generations. The source’s approximately 19-fold and 1.2-fold overhead claims are not supported by a consistent evaluation count or supplied timing traces.

A possible noisy-objective extension averages repeated measurements before calculating improvements. If independent Gaussian observations z₁,…,z_k of a scalar mean have variance σ_g² and the prior is N(μ₀,σ₀²), the conjugate posterior mean is

μ_post=(σ₀⁻²μ₀+σ_g⁻²Σℓzℓ)/(σ₀⁻²+kσ_g⁻²). (8)

This illustrative model is not automatically a model for the clipped, correlated improvement scores in Eq. (3). Repeated evaluations consume budget, and noise in parent and offspring values affects credit bias. No noisy-objective result is established by the supplied experiment.

A possible multi-objective extension defines a parent-level dominance reward, counting offspring that dominate their corresponding parents, and uses an explicitly specified Pareto archive. It would require independent archive, diversity and budget validation. The single-objective table does not test convergence to a Pareto front.

Operators, folds and candidate evaluations can be processed concurrently if their state is isolated from the shared snapshot. Concurrency may reduce elapsed time but does not reduce the number of objective calls. Speedups require measured scheduling, communication and timing data; no 64-core speedup is certified here.

Proposition 1. Let f★ be finite and retain an elitist incumbent best value b_m over all evaluated candidates. Suppose that, for every ε>0 there is qε>0 such that, at each of m eligible proposal trials, the conditional probability of generating a point in Aε given the entire previous history is at least qε. Then

Pr(b_m>f★+ε) ≤ (1−qε)^m. (9)

Proof: Before the first hit, the conditional miss probability at each eligible trial is at most 1−qε. Repeated conditional expectation bounds the probability of m consecutive misses by their product. After a hit, elitist retention keeps the incumbent at most f★+ε. Independence of trials is unnecessary. Taking m→∞ and applying the argument to ε=1/n for all positive integers n gives b_m→f★ almost surely when eligible trials continue indefinitely. This is conditional asymptotic coverage, not a conclusion from the finite source runs.

A sufficient condition is a selected operator with a restart component of conditional probability at least ρ>0 and proposal measure ν satisfying ν(Aε)>0, together with π_j≥μ/K. Then qε may be bounded below by (μ/K)ρν(Aε). The portfolio labels do not establish the restart component or its support.

qε ≥ (μ/K)ρν(Aε) > 0, under the stated restart and sublevel-set assumptions. (10)

Uniform exploration over operator labels is weaker than exploration over candidate locations. For a merely measurable function, an isolated lower-valued point may have zero proposal measure, so even a uniform restart need not approach the ordinary infimum. The positive-sublevel-probability assumption is therefore substantive.

The incumbent gap Y_m=b_m−f★ is nonnegative and nonincreasing for exact fixed-objective comparisons. If integrable, it is a supermartingale. Optional stopping at a bounded stopping time τ gives:

E[Y_τ] ≤ E[Y₀], for bounded τ and an integrable incumbent gap. (11)

This inequality alone does not quantify progress toward the optimum. A concentration inequality controls deviation from an expectation; it cannot eliminate an unknown optimization bias. No O(1/√(NT)) objective-error bound follows from bounded differences and Lipschitz continuity without a quantitative search-coverage argument.

Fixed-forgetting-factor smoothing is not a cumulative exponential-weights rule. Even constant rewards can leave positive probability on an inferior operator, and the uniform mixture deliberately incurs continued exploration cost. For constant rewards with gap Δ>0, uniform mixing alone can contribute expected regret at least (μ/K)Δm relative to always selecting the better operator. Thus a vanishing average regret claim would require a different comparator, a diminishing exploration schedule or an independently analyzed update. The finite benchmark table measures final objective errors and does not empirically prove a bandit regret rate.

A bound on the spectral radius of a population covariance matrix concerns dispersion, not the Jacobian of a population-update map. It does not imply local contraction of operator dynamics. Stability of a random switching system would require assumptions on the operators and their shared state that are absent from the source formulation. The current theory consequently makes no local spectral-stability claim. Its only optimization guarantee is the conditional hitting statement, whose restart support and unlimited-trial assumptions must not be attributed to the finite implementation without verification.

The source describes three benchmark campaigns; only its selected CEC 2017 endpoint table is supplied in full:

The principal supplied table contains F01–F25 at d=30. The source reports exclusion of F26–F30 because of numerical difficulties in two baselines; the missing failure logs and exclusion timing prevent assessment of selection bias. The comparison applies to the selected set, not to all CEC 2017 cases or an official competition ranking. The modified official suite removes F2; the included F02 is therefore a source-specific variant requiring code identification [13].

The source additionally describes a 12-function CEC 2022 campaign at d=10 and d=20 [14]. Its complete per-function results and evaluation logs are not supplied, so it is a reported extension rather than an independently inspectable validation result.

A BBOB campaign with 24 functions at six dimensions and 15 runs is also described [16]. Its instance identifiers, complete tables and outputs are needed before cross-suite transfer can be assessed.

Eight state-of-the-art baselines are compared:

L-SHADE [10] uses success-history adaptation and linear population-size reduction.

jSO is the named adaptive differential-evolution comparator.

NL-SHADE-RSP [11] uses nonlinear reduction and rank-based selective pressure.

AGSK is the named gaining-sharing comparator.

EBOwithCMA is the named ensemble comparator.

CMA-ES denotes the supplied covariance-adaptation implementation.

IPOP-CMA-ES denotes the supplied increasing-population restart implementation.

MADDE denotes the supplied multi-adaptive differential-evolution implementation.

The source reports irace tuning [9] with 5,000 runs on five CEC 2017 functions outside the displayed test set. Function identities, configuration spaces, baseline versions and tuning expenditures are necessary to verify separation from the test results. Tuning calls are external development costs and must be reported separately from run budgets.

The source reports 51 runs per function and algorithm, common seed indices and budgets of 10⁴d, 5×10⁴d and 10⁵d calls for CEC 2017, CEC 2022 and BBOB, respectively. Shared seed labels do not by themselves prove identical initial populations, especially for implementations with different population sizes. The actual initialization mapping and call counter, including probes, must be reconciled before equal-budget or paired-run claims are accepted.

The supplied summaries are retained, but their statistical input units and arithmetic require reconstruction. A problem-level analysis should use one prespecified performance summary per algorithm and function; a run-level paired analysis requires the corresponding matched observations and dependence structure. Table 2 retains displayed final-error means and parenthetical standard errors. The source’s raw-versus-log transformation choices are not fully mapped to functions. Recomputing tests requires the unrounded observations and exact transformations. Table 5 retains selected reported confidence intervals. The source specifies 1,000 percentile-bootstrap resamples; without resampling arrays and scripts, coverage and resampling units cannot be checked. Friedman comparisons [17] and their interpretation across problems [3] require the complete rank matrix. For N independent comparison blocks and a algorithms, Nemenyi’s critical difference is CD=qα√[a(a+1)/(6N)] [6]. The qα convention and multiplicity family must be stated.

Wilcoxon signed-rank tests [25] require paired differences with a stated treatment of zeros and ties. Holm’s step-down correction [26] and Bonferroni correction must use the same declared family of eight contrasts. Cohen’s d [18] is a standardized mean difference. Its sign and denominator must be defined before pooling heterogeneous objective scales; categorical magnitude labels are descriptive conventions. A₁₂ [4] is defined here in the favorable direction as Pr(error_AOP<error_baseline)+½Pr(tie). Values near 0.5 indicate little stochastic ordering. Under the source’s thresholds, 0.68 is medium rather than large. Bootstrap effect-size intervals require the unrounded paired or independent arrays appropriate to the chosen estimator [19], [20]. Observed-effect post-hoc power is a transformation of the observed result and does not independently establish adequate study sensitivity. Equivalence requires a prespecified margin and two valid one-sided tests on a defined estimand. A failed difference test is not evidence of equivalence; a failed equivalence test is not evidence of superiority. The supplied TOST entries remain unresolved outputs rather than verified non-inferiority findings.

RSP F01 1.23 (0.06) 1.34 (0.10) 1.48 (0.09) 1.71 (0.11) F02 1.07 (0.13) 0.91 (0.10) 1.62 (0.38) 1.55 (0.18) F03 0.015 (0.003) 0.035 0.057 0.049 (0.007) (0.005) (0.010) F04 4.21 (0.32) 3.18 (0.21) 2.95 (0.18) 3.55 (0.27) F05 6.74 (0.51) 9.12 (0.72) 11.45 (1.05) 13.21 (1.22) F06 0.42 (0.04) 1.31 (0.10) 1.85 (0.13) 1.78 (0.12) F07 1.95 (0.15) 1.21 (0.09) 1.42 (0.10) 1.78 (0.13) F08 0.021 (0.004) 0.041 0.058 0.052 (0.007) (0.006) (0.008) F09 2.85 (0.21) 4.15 (0.32) 5.21 (0.41) 4.95 (0.36) F10 5.32 (0.40) 2.95 (0.21) 4.12 (0.31) 4.51 (0.33) F11 0.0034 0.018 0.025 0.021 (0.003) (0.0006) (0.003) (0.004) F12 0.18 (0.02) 0.31 (0.04) 0.45 (0.05) 0.42 (0.04) F13 0.082 (0.011) 0.121 0.181 0.155 (0.018) (0.015) (0.022) F14 3.85 (0.30) 2.92 (0.21) 3.18 (0.24) 3.45 (0.27) F15 1.25 (0.10) 1.95 (0.15) 2.45 (0.19) 2.21 (0.17) F16 0.42 (0.05) 0.71 (0.08) 0.95 (0.11) 0.85 (0.09) F17 2.81 (0.22) 2.95 (0.24) 3.21 (0.26) 3.18 (0.25) F18 0.012 (0.002) 0.025 0.041 0.035 (0.005) (0.004) (0.006) F19 0.45 (0.04) 0.71 (0.06) 0.95 (0.08) 0.85 (0.07) F20 0.95 (0.08) 1.51 (0.12) 1.95 (0.16) 1.78 (0.14) F21 5.21 (0.42) 4.85 (0.38) 5.41 (0.44) 5.32 (0.42) F22 0.082 (0.010) 0.181 0.241 0.215 (0.027) (0.022) (0.030) F23 1.95 (0.15) 1.21 (0.09) 1.61 (0.12) 1.51 (0.11) F24 0.18 (0.02) 0.41 (0.05) 0.61 (0.07) 0.55 (0.06) F25 1.21 (0.10) 1.71 (0.14) 2.21 (0.18) 2.05 (0.16) CMA CMA-ES 1.42 (0.08) 2.10 (0.13) 1.92 (0.11) 2.30 (0.15) 1.79 (0.10) 1.20 (0.12) 1.34 (0.11) 1.18 (0.09) 1.61 (0.21) 1.41 (0.13) 0.028 0.061 0.040 0.072 0.052 (0.004) (0.008) (0.005) (0.011) (0.006) 3.21 (0.20) 4.85 (0.35) 3.92 (0.29) 5.21 (0.40) 3.71 (0.24) 8.95 (0.68) 14.21 11.85 15.42 12.51 (1.10) (1.31) (0.98) (1.45) 1.21 (0.09) 2.15 (0.15) 1.62 (0.11) 2.41 (0.18) 1.71 (0.13) 1.31 (0.09) 1.85 (0.13) 1.51 (0.11) 2.12 (0.16) 1.62 (0.12) 0.034 0.072 0.045 0.081 0.054 (0.005) (0.010) (0.006) (0.012) (0.007) 3.65 (0.27) 6.42 (0.51) 5.18 (0.40) 7.15 (0.58) 5.51 (0.42) 3.41 (0.25) 6.85 (0.55) 4.92 (0.37) 7.21 (0.61) 5.21 (0.42) 0.012 0.031 0.018 0.038 0.022 (0.002) (0.005) (0.003) (0.006) (0.004) 0.28 (0.03) 0.62 (0.07) 0.38 (0.04) 0.71 (0.08) 0.41 (0.04) 0.118 0.215 0.142 0.241 0.165 (0.014) (0.027) (0.017) (0.030) (0.019) 2.81 (0.19) 4.25 (0.34) 3.62 (0.28) 4.51 (0.36) 3.35 (0.25) 1.71 (0.13) 2.85 (0.22) 2.12 (0.16) 3.21 (0.25) 2.32 (0.18) 0.65 (0.07) 1.21 (0.14) 0.82 (0.09) 1.35 (0.16) 0.91 (0.10) 2.75 (0.21) 4.21 (0.34) 3.41 (0.28) 4.51 (0.37) 3.32 (0.27) 0.021 0.055 0.030 0.062 0.038 (0.003) (0.008) (0.004) (0.009) (0.005) 0.65 (0.05) 1.21 (0.11) 0.82 (0.07) 1.35 (0.13) 0.91 (0.08) 1.32 (0.10) 2.21 (0.19) 1.71 (0.13) 2.45 (0.21) 1.81 (0.15) 4.51 (0.34) 7.21 (0.62) 6.15 (0.51) 7.85 (0.68) 6.41 (0.52) 0.151 0.312 0.201 0.351 0.231 (0.018) (0.040) (0.024) (0.045) (0.028) 1.18 (0.09) 2.21 (0.18) 1.71 (0.13) 2.41 (0.20) 1.81 (0.14) 0.35 (0.04) 0.75 (0.09) 0.51 (0.06) 0.85 (0.10) 0.62 (0.07) 1.51 (0.12) 2.51 (0.21) 2.12 (0.17) 2.81 (0.24) 2.21 (0.18)

The source reports Python 3.11, NumPy 1.26 and SciPy 1.13 on AMD EPYC 7763 hardware with Ubuntu 22.04. The environment, Dockerfile and workflow have not been supplied with the manuscript, so these descriptions remain author-reported execution information.

The reported defaults are K=9, k=5, τ_probe=5, η=0.5, λ=0.85, μ=0.10, N=100 and ρ₀=1. In this notation η is inverse temperature and μ is the uniform exploration mixture. The exact operator parameters and the executed probing rollout remain part of the required implementation record.

Counting the smallest displayed mean in each row of Table 2 gives 17 AOP-KFP minima, three for jSO, four for EBOwithCMA and one for L-SHADE. This corrects the source narrative’s 14/7/3/1 tally. Row minima are descriptive outcomes at the displayed precision and do not imply per-function statistical superiority.

The supplied mean ranks favor AOP-KFP at 2.44 and sum to 45, the required total for nine algorithms. This necessary check does not establish that they were derived from Table 2. The supplied χ²=78.38 and p=1.04×10⁻¹³ need reconciliation with the unrounded rank matrix, ties and comparison unit.

The source reports Friedman χ²(8)=78.38 and p=1.04×10⁻¹³; these values are retained as unresolved reported outputs.

Nonsignificance does not establish equivalence.

Using the source-supplied CD=3.40 solely as a conditional threshold, AOP-KFP differs by more than that threshold from AGSK, CMA-ES and MADDE. It does not exceed that threshold against jSO, EBOwithCMA, L-SHADE, IPOP-CMA-ES or NL-SHADE-RSP. The supplied diagram is an illustration whose threshold and inputs still require reconstruction.

The AOP-KFP–IPOP-CMA-ES difference is 5.48−2.44=3.04, below 3.40.

The AOP-KFP–NL-SHADE-RSP difference is 5.56−2.44=3.12, also below 3.40.

Pairwise nonsignificance is not transitive and must not be summarized as three disjoint equivalence cliques. Consequently, even accepting the source threshold does not support the original claim of five significant Nemenyi contrasts. Confirmatory post-hoc conclusions await the validated rank matrix and critical-value calculation.

Table 4 preserves the source’s paired-test, correction and effect-size outputs. Several corrected entries cannot be obtained from the displayed raw p-values for one family of eight tests. For example, Bonferroni correction of 0.003 is 0.024, not the displayed 0.064. Statistical decisions cannot be certified from these unresolved columns.

The displayed A₁₂ values range from 0.68 to 0.96; 0.68 is medium under the stated thresholds, while the other seven are large. The Cohen’s d values lie between 0.25 and 0.50, with 0.50 on the chosen category boundary. These different estimands can give different magnitude descriptions. Seven displayed d intervals exclude zero, but their validity depends on the resampling and aggregation protocol. Neither those intervals nor observed-effect power resolves the correction errors.

Table 5 retains selected source confidence intervals on mean error. Complete bootstrap inputs are needed to establish whether functions, runs or another unit were resampled and whether the intervals correspond to the Table 2 metric.

The supplied post-hoc power values range from 0.22 to 0.67. They do not constitute an independent design-sensitivity analysis, and low values do not predict that a larger experiment would necessarily reveal a difference. Future sample-size planning should use prespecified practically relevant effects and a defined comparison unit.

The TOST columns are retained as source outputs. Equivalence of a standardized difference within ±0.5 and one-sided non-inferiority are distinct hypotheses. The tested estimand, standardization, confidence level and one-sided p-values must be supplied before either claim is made. A TOST failure for CMA-ES does not itself establish superiority.

The source reports additional CEC 2022 ranks and BBOB dimension-dependent comparisons, but their complete tables are absent from the supplied manuscript. These descriptions identify follow-up validation material; they are not used here to establish cross-suite superiority or transferability.

The supplied curves depict early descent and changing relative ordering on four selected functions. A confidence band for a median is uncertainty about that summary, not directly the distribution of run outcomes. The plotted endpoints are not a substitute for the numerical endpoint table and must be mapped to the same metric and evaluation budget.

The reported frequencies sum to 100%, ranging from 7% for the PSO label to 18% for DE/rand/1. A broad pooled distribution can coexist with concentration in individual runs or stages. The figure therefore describes aggregate usage rather than proving that the exploration mechanism prevented collapse.

The source describes an operator-count sweep from K=1 to K=12, but does not supply its result arrays, redundant-operator definitions or probe-adjusted budgets. Its claimed preferred K and percentage changes are not treated as independently supported tuning results.

A decay sweep is also described without complete outputs. Smoothing trades responsiveness against variability, but the optimum λ cannot be established from the provided ablation table alone.

The source reports 2,048 evaluations for a Sobol analysis of six hyperparameters on eight selected functions. Valid variance-based sensitivity indices require a defined scalar response, parameter distribution, sampling scheme and estimator. Those inputs and estimation uncertainties are not supplied.

The first-order entries sum to 1.16. For a standard variance decomposition with independent inputs and a correctly defined response, population first-order indices sum to at most one. Finite-sample estimation error or an incompatible setup could explain the discrepancy, but the supplied material does not identify which. Subtracting the sum of first-order indices from the sum of total-order indices is not the total interaction variance, because interactions are counted repeatedly in total-order indices. These numbers therefore do not establish either interaction strength or robust defaults.

The claimed flat performance surface within ±30% of defaults is not accompanied by a response grid. A deployment range requires measured performance, cost and uncertainty over the stated parameter distributions, not an inference from unresolved sensitivity estimates.

The mechanism makes allocation decisions interpretable through local credits and selection probabilities. The displayed endpoint table offers descriptive evidence of favorable means on the selected functions. Its stronger advantages, low variability, transferable defaults and superiority over competitors, require the missing outputs and corrected inferential calculations.

Synthetic benchmarks do not establish performance under observation noise, changing objectives, equality constraints or mixed-integer design requirements. The source mentions three supplementary engineering problems without complete results or feasibility records; those mentions do not mitigate the present evidence limits. Named baselines must be tied to exact versions and configurations. A later CEC-winner analysis [16] can motivate further comparisons, but implementation availability and the source experiment’s chronology require author documentation.

The identity of the five tuning functions and their relationship to the omitted test functions are unresolved. Tuning and exclusion decisions must be documented before transfer across suites is interpreted; missing supplementary tables cannot provide independent validation.

Raw error, log error and rank summaries answer different questions. Combining them without a function-level transformation map can change effects and test outcomes. The discrepancy between displayed means and supplied summary analyses must be resolved from unrounded data rather than by replacing original numerical cells.

Correct multiplicity control [26], [27] depends on a declared family and valid raw tests. The supplied correction columns contain arithmetic inconsistencies, and no Benjamini–Hochberg robustness output is provided. Inference remains conditional on rebuilding the analysis from its original observations.

Probe calls are a substantial part of the optimization budget, especially when objective evaluations are expensive. Parallel scheduling reduces elapsed time only when measured; it does not make extra calls negligible. Reporting both actual calls and elapsed time is necessary to distinguish sample efficiency from throughput.

The table’s losses occur on F02, F07 and F10 against jSO, F04 against L-SHADE, and F14, F17, F21 and F23 against EBOwithCMA. These observations are compatible with landscape-dependent operator usefulness, but do not identify which internal component caused the losses. A nonzero exploration floor also imposes deliberate opportunity costs when one operator remains best.