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Candidate Comparability Before Promotion: Conditional Validation in Adaptive Network Intrusion Detection

Roberto Fernández-Barrios, Iker Pastor-López, Amaia Pikatza-Huerga, Pablo García Bringas

arXiv:2609.04388v1cs.CRcs.LG

TL;DR

A drift alarm proposes an update but does not establish that a challenger should replace the incumbent, a security-relevant promotion decision. The paper tests how candidate construction and evidence affect promotion using controlled challenger pipelines, size controls, policy comparisons, and feature-disjoint evaluation. Results show benchmark-dependent gains from greater candidate evidence and conditional, rather than universal, benefits from validation.

  • Problem

    A drift alarm detects distribution change but does not establish whether a particular challenger is sufficiently supported to replace the deployed incumbent.

    Source: §1 · p. 1, §3.1 · p. 4

  • Method

    The study uses self-contained challenger pipelines, controlled candidate-evidence comparisons, a common-harness update-policy comparison, and exact-feature-disjoint role assignment.

    Source: §1 · p. 2, §4.2.1 · p. 9, §5.3 · p. 14

  • Results

    With exact-feature-disjoint roles, 512→2,000 samples per class yielded +0.53, +1.67, and +0.38 balanced-accuracy points, positive but benchmark-dependent.

    Source: §6 · p. 22, §8 · p. 25

  • Takeaways & Limitations

    Candidate construction and evidence should be controlled, reported, and interpreted explicitly because promotion conclusions and policy rankings are conditional on them.

    Source: §6 · p. 22

    Validation assumes a small labeled probe; under random inspection its harm-regime protection dissolves at π = 0.01, and candidate-aware label-flipping adversaries remain untested.

    Source: §7 · p. 25

Abstract

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Adaptive network intrusion detection systems retrain classifiers after drift alarms, but an alarm detects change; it does not establish that a challenger should replace the deployed incumbent. Promotion is security-relevant because it changes the model responsible for subsequent attack detection, and evaluating it has a methodological problem: promotion conclusions may depend on how the challenger was constructed and on how much evidence supports it. We test that dependence on CICIDS2017, UNSW-NB15 and ToN-IoT with self-contained challenger pipelines, nested candidate-size controls, a common-harness comparison of nine update policies, and a final sensitivity confining every exact feature vector to one evaluation, training or probe role. Incumbent-owned frozen preprocessing amplified apparent promotion harm; with self-contained challenger pipelines the mean full-drift harm did not persist. Raising nominal candidate evidence from 512 to 2,000 samples per class improved promotion under pool-constructed progressive drift by +0.53, +1.67 and +0.38 balanced-accuracy points: positive and statistically resolved in all three benchmarks, but materially benchmark-dependent rather than homogeneous, and driven mainly by fewer false positives. Policy conclusions were partially robust: policy ordering changed with candidate comparability, no policy globally dominated, and earlier compatibility statements for a label-free estimator and a calibrated ensemble narrowed. Validation helped evidence-disadvantaged challengers but added no average benefit at parity. Thirteen replays on real, time-ordered traffic showed no net harm from always deploying. Challenger construction and evidence should be controlled, reported and interpreted explicitly when promotion is evaluated.

1 Introduction

Drift detection proposes retraining, but does not establish that a particular challenger should replace the incumbent. The paper argues that promotion conclusions depend on candidate construction and evidence, and tests those conditions with controlled comparisons.

1 Introduction

  • A drift alarm detects change, not whether a challenger should replace the incumbent in this security-relevant decision.Promotion changes the model responsible for subsequent attack detection.Source: §1 · p. 1
  • The study combines controlled replications, candidate-size controls, a common-harness policy comparison, and a final exact-feature-disjoint sensitivity.“Pre-specified” and “preregistered” refer to protocols specified and version-controlled before each stage’s confirmatory seeds, not external registration of the sequential study as a whole.Source: §1 · p. 2
  • Promotion conclusions and update-policy rankings depend on challenger construction and evidence, motivating an explicit comparability audit before decisions are interpreted.The paper decomposes updating into trigger, construction, evidence comparability, optional validation, promotion, and future deployment outcome.Source: §1 · p. 2
  • Removing incumbent-owned frozen preprocessing eliminated mean full-drift harm, while raising nominal evidence from 512 to 2,000 per class retained a positive, benchmark-dependent benefit.The evidence-size effect was positive and statistically resolved in all three benchmarks under pool-constructed progressive drift.Source: §1 · p. 2
  • Validation helped asymmetric challengers but showed no detectable average benefit once challengers were self-contained and evidence-matched.The latter result held at zero drift and under drift; strict validation had a measurable cost in one cell.Source: §1 · p. 2
  • Thirteen chronological replays and a quantum-kernel monitor served as supporting boundary checks, not universal policies or primary contributions.The replays showed no net harm from always deploying but did not estimate deployment frequency.Source: §1 · pp. 2–3

2 Related work

Related work addresses drift monitoring, online adaptation, security evaluation, and validation-gated updates, but generally does not make per-proposal incumbent–challenger promotion its decision unit. The paper positions candidate comparability as an experimentally controlled factor in that decision.

2 Related work

  • Adaptive NIDS systems address online or scheduled response to drift, but the cited systems do not perform the same per-proposal incumbent–challenger promotion comparison.Examples include CARAVAN, SPIDER, NOCTOWL, SSF, and ADAWU-IDS.Source: §2 · p. 3
  • Distribution-level detectors trigger retraining but do not account for model degradation, and changing detector family did not change evaluated promotion outcomes.The common-harness comparison included reference DDM and ADWIN implementations; the quantum-kernel monitor was only a detector-invariance check.Source: §2 · p. 3
  • Security-evaluation research documents temporal and experimental bias, while adjacent update studies examine pseudo-label degradation and label-selection dependence.The cited evaluation work includes TESSERACT, Arp et al., Apruzzese et al., and Jacobs et al.; update studies include Kan et al. and Chen et al..Source: §2 · p. 3
  • Validation gates, champion–challenger evaluation, and label-efficient comparison are established approaches; the paper’s contribution is testing comparability’s effect on per-proposal promotion in adaptive NIDS.The study makes no head-to-head superiority claim against formulations with different objectives, information sets, and outputs.Source: §2 · p. 4

3 Candidate promotion as a decision pipeline

The promotion pipeline separates detecting change from deciding whether a particular challenger should replace the incumbent. Construction and evidence establish comparability before optional validation and promotion.

3.1 Promotion as a sequential decision

  • A labeled probe estimates the contemporaneous candidate–incumbent difference as a surrogate for future value, which is generally unobserved at decision time.The probe is not an observation of the candidate’s realized future value.Source: §3.1 · p. 4

3.2 Drift monitors

  • The study uses two-sample monitors including Energy distance, RBF-MMD, Kolmogorov–Smirnov, Jensen–Shannon divergence, and quantum-kernel MMD as a detector-invariance check.Thresholds are calibrated per detector at the 0.95 quantile, and the paper’s claims are detector-agnostic.Source: §3.2 · p. 4

3.3 Pool-constructed progressive-drift readaptation protocol

  • Pool-constructed progressive drift mixes empirical reference and current-regime pools, ramping severity from 0 to 1 over 80 of 100 post-drift windows.The trigger policy is fixed across gate conditions, and confirmatory arms process bit-identical streams.Source: §3.3 · p. 5

3.4 The validate-before-commit gate

  • The deployment gate decides whether a trained challenger replaces the incumbent; point validation accepts any observed probe advantage, while risk-controlled gates require statistical evidence.The stated guarantee concerns false probe-superiority under a conditional null, not future deployment harm.Source: §3.4 · p. 5, §3.5 · pp. 6–7

4.1 Datasets and controlled streams

The controlled study spans three intrusion-detection benchmarks and uses paired streams to compare update conditions. Confirmatory claims rely on a hardened harness, while the initial exploratory results are treated as context.

4.1 Datasets and controlled streams

  • CICIDS2017, UNSW-NB15, and ToN-IoT cover benefit, marginal or mixed, and harmful readaptation regimes, with one primary confirmatory scenario per benchmark.The authors treat CICIDS2017 as the benefit end of a three-benchmark spectrum; the marginal and harmful regimes come from UNSW-NB15 and ToN-IoT.Source: §4.1 · p. 8
  • The confirmatory harness pre-generates bit-identical streams for every arm and uses source-row-disjoint partitions, separate random generators, and per-trigger logging.A final sensitivity changes the partitioning to make exact feature vectors disjoint across roles.Source: §4.1 · p. 8
  • The replication protocol was committed before confirmatory runs, which used 30 held-out seeds untouched by smoke tests.The earlier exploratory arms were seed-matched but unpaired, and their results are context because claims were re-established with fresh seeds.Source: §4.1 · pp. 8–9
  • Historical candidates used 512 balanced flows per class, while initial models used 2,000 per class; latency arms shift probe or candidate data to earlier windows.The candidate trains on the current mixture, a simulator convenience unavailable to production systems; probe labels are incremental to retraining labels.Source: §4.1 · p. 8

4.2 Candidate construction and evidence controls

The controls isolate how challenger construction and nominal evidence size affect promotion outcomes. Each replication changes a pre-specified factor while holding other conditions fixed.

4.2 Candidate construction and evidence controls

  • The staged controls isolate preprocessing ownership and candidate-evidence size under distinct drift regimes, with protocols and interpretation rules frozen before confirmatory seeds ran.The controls were specified sequentially but presented by factor and drift regime rather than chronology.Source: §4.2 · p. 9

4.2.1 Transformer ownership: self-contained candidate pipelines

  • The ownership replication compares frozen initial preprocessing with self-contained challenger pipelines while keeping raw candidate batches and monitoring policy fixed.Each self-contained challenger fits its own scaler and PCA on its candidate batch; neither probe nor future windows enter a fit.Source: §4.2.1 · p. 9

4.2.2 Candidate evidence size at zero drift: the size-matched control

  • The zero-drift size-matched control changes challenger training size from 512 to 2,000 samples per class while retaining the 2,000-per-class incumbent.The 512-sample batch is nested as the prefix of the 2,000-sample batch; draws are with replacement, so nominal size does not guarantee equal effective information.Source: §4.2.2 · p. 10

4.2.3 Candidate evidence size under pool-constructed progressive drift

  • The progressive-drift control repeats the nested size intervention at matched proposal-time severity, comparing 512- and 2,000-per-class challengers across three full-drift scenarios.Thirty fresh seeds were used, and the two always-deploy arms shared trigger and commit timelines.Source: §4.2.3 · p. 10

4.3 Promotion policies and the common-harness comparison

The common-harness comparison evaluates promotion and retraining alternatives under shared streams and self-contained challengers. The design documents method-specific information budgets and limits conclusions about untuned reference monitors to their evaluated configurations.

4.3 Promotion policies and the common-harness comparison

  • The comparison includes anchor policies, label-free accuracy estimators, retraining baselines, and DDM and ADWIN reference triggers on bit-identical raw streams.The reference monitors use registered parameters and eight monitoring labels per window; their cells are evidence about those configurations, not the methods generally.Source: §4.3 · p. 11
  • Nine update-policy alternatives are compared at nominal 2,000-per-class evidence parity, with a secondary 512-per-class sensitivity for six policies.The primary comparison uses six scenarios, 96 arms, and 30 fresh seeds.Source: §4.3 · p. 11
  • No faithfully reproducible end-to-end published adaptive-NIDS system matched the same decision problem and information interface, and no evaluated row is labelled state of the art.Method-specific information budgets are documented rather than equalized.Source: §4.3 · p. 11

4.4 Exact-cleaned-feature-disjoint integrity sensitivity

An audit found exact cleaned feature vectors crossing source-row-separated roles. The final sensitivity assigns each exact-X group to a single role and repeats the full-drift size and common-harness blocks.

4.4 Exact-cleaned-feature-disjoint integrity sensitivity

  • Exact cleaned feature vectors crossed roles despite source-row splitting; beyond the first member of an exact-X group, row shares were 13.63%, 36.41%, and 11.23% across the three scenarios.UNSW-NB15 contained 403 conflicting-label groups involving 1,828 rows; every original row and label was retained.Source: §4.4 · p. 11
  • The final protocol assigns every exact-X group to one role, preserving all rows, multiplicity, and contradictory labels while guaranteeing no exact-feature overlap across evaluation, training, and probe roles.All role audits passed, with zero cross-role exact-X overlap and maximum stratum-fraction deviation 0.0058 percentage points.Source: §4.4 · p. 11
  • The sensitivity repeats the full-drift size-control and common-harness blocks on fresh seeds, using pre-frozen robustness classifications and comparison rules.Grouping used features only, and no parameter changed after execution began.Source: §4.4 · pp. 11–12

4.5 Outcomes and inference

The study measures stream-level outcomes with balanced accuracy as its primary endpoint and uses paired, seed-clustered inference. Its evidence hierarchy distinguishes final claims from mechanism, cost, and boundary analyses.

4.5 Outcomes and inference

  • Balanced accuracy is the primary endpoint, averaged across 100 windows per stream and then across seeds; attack recall and false-positive rate are safety guardrails, not verdicts.Probe-level guarantees do not guarantee future deployment outcomes.Source: §4.5 · p. 12
  • Confirmatory comparisons use bit-identical pre-generated streams and seed-clustered bootstrap confidence intervals, while windows, triggers, and commits are not treated as independent units.Harmful-proposal summaries are descriptive within-trajectory fractions over seed-clustered commits.Source: §4.5 · p. 12
  • The final claims rely on the exact-feature-disjoint sensitivity; other evidence blocks test mechanisms, costs, or boundaries.The evidence hierarchy and block provenance are catalogued in the supplementary resource.Source: §4.5 · p. 12

5 Results

The results examine how challenger construction, candidate evidence, and validation shape promotion outcomes across controlled comparisons and chronological replays. Larger candidate evidence improved balanced accuracy in all three benchmarks, with benefits varying by benchmark and policy ordering depending on candidate size; validation helped evidence-disadvantaged challengers but added no average benefit at parity, and always-deploy showed no observed net harm in the replays.

5 Results

  • The originally reported ToN-IoT result was +1.03 [0.55, 1.53] and Holm-significant; full-drift harm was configuration-dependent and strongly amplified by incumbent-owned preprocessing.On ToN-IoT full drift, the ownership interaction was +5.98 [3.82, 8.26].Source: §5.2 · p. 13
  • At zero drift, increasing candidate size from 512 to 2,000 per class improved balanced accuracy by +1.89 on PortScan, +0.63 on UNSW, and +0.23 on ToN-IoT.The 512-per-class challengers reproduced harm, whereas matched-size mean effects were compatible with the ±0.5-point margin; nominal size parity does not establish parity in effective information or temporal coverage.Source: §5.3 · p. 14
  • The evidence-size results isolate nominal row count within nested pool samples, but do not establish effective information parity or a universal benefit from more data.Pool draws can contain duplicates and do not equate temporal span, diversity, subtype support, or information content; the source-row-disjoint full-drift estimate is superseded by the exact-feature-disjoint sensitivity.Source: §5.3 · pp. 14–15, §5.4 · p. 15
  • Under exact-feature-disjoint evaluation, increasing candidate size from 512 to 2,000 per class improved full-drift balanced accuracy by +0.53, +1.67, and +0.38 on PortScan, UNSW-Recon, and ToN-IoT, respectively.These are the governing estimates; they narrow the earlier source-row-disjoint result, which had been classified as a homogeneous size benefit.Source: §5.4 · p. 15

5.5 Validation has conditional average value

  • Validation improved outcomes when challengers had 512 samples per class, but provided no average benefit at 2,000-per-class parity under zero drift or full drift.At 512/class, strict validation gains over always-deploy under zero drift were +1.68 [1.23, 2.13] on PortScan, +0.51 [0.38, 0.64] on UNSW, and +0.34 [0.20, 0.49] on ToN; under full drift, its ToN-IoT gain was +0.64 [0.26, 1.06] while its UNSW-Recon effect was −0.21 [−0.36, −0.06].Source: §5.5 · pp. 15–16
  • At parity, validation adds no average benefit, while full-drift “pays for it” results hold for DoC, replay, DDM and ADWIN, but not ATC or the calibrated ensemble.ATC is compatible with always-deploy on UNSW-Recon and ToN-IoT but unresolved on PortScan; the calibrated ensemble is compatible in all three. DDM and ADWIN were evaluated at registered reference parameters, and both monitors consume 800 monitoring labels per stream.Source: §5.6 · p. 17, §5.7 · p. 18
  • Policy ordering depends on candidate size: all 15 Holm-significant method-by-size interactions are negative, and the pre-specified ordering-change rule fires for ATC and the calibrated ensemble.The rule does not fire for point, strict or DoC; no evaluated policy globally dominates, and the paper’s final interpretation is that policy rankings remain conditional on challenger construction and evidence.Source: §5.6 · p. 18, §5.7 · p. 19
  • +0.53, +1.67 and +0.38 balanced-accuracy points: 2,000/class beats 512/class in PortScan, UNSW-Recon and ToN-IoT, respectively, under exact-feature-disjoint roles.All three effects are Holm-resolved; PortScan and UNSW meet the pre-specified materiality rule, while ToN-IoT is sub-material. The verdict is partial robustness, not a homogeneous benefit; seed effects are heterogeneous around the PortScan margin.Source: §5.7 · p. 18, Table 9 · p. 19

5.8 Mechanism, formal instruments and external boundaries

  • The lifetime-budgeted pooled sequence recovers 93% of always-deploy’s benefit at cap 512, while the deployment-long stratified guarantee reaches 81%.The formal guarantee controls false establishment of probe superiority under the conditional weak null, not future deployment harm; the empirical gates had zero observed harmful updates over 506 evaluable commits versus 39% for always-deploy, which provides no population-rate bound.Source: §5.8 · p. 20
  • Across 13 chronological replays, always-deploy never lost to never adapting, but this is absence of observed harm, not an estimate of harm frequency.On CICIDS streams where incumbents collapsed, retraining recovered +13.6 to +43.8 balanced-accuracy points; formal VBC-SG-Cohort-sim retained only 0–9% of always-deploy recovery on five CICIDS replays, versus 91% and 129% on two healthy UNSW timelines.Source: §5.8 · p. 20, Table 11 · p. 21
  • Incumbent degradation predicts future commitment value (regime-specific r = −0.67 to −0.70), while detector score shows no consistent association (r = −0.01 to +0.05).The mixed-effects model identifies degradation as the only predictor whose CI95 consistently excludes zero (βdeg = −1.02 [−1.61, −0.43] per BA point); the association is descriptive, not causal.Source: §5.8 · p. 19, Figure 3 · p. 21
  • Alert-enriched inspection cuts label-search effort 5–8×, but gate protection dissolves at prevalence π = 0.01, where two-thirds of 32-flow probes contain no attack.The gate holds down to π ≈ 0.05; the binding constraint at π = 0.01 is a starved trigger, not the gate.Source: §5.8 · p. 21

6 Discussion

Promotion conclusions and policy rankings depend on challenger construction and evidence, while validation and deployment context delimit what the results support. The discussion finds conditional benefits rather than a universally best update or validation policy.

6 Discussion

  • Across seven registered chronological replays, no stream showed net harm; gates preserved some recovery on collapsed-incumbent streams but the comparisons were descriptive.Healthy-stream point estimates favored point and strict gates on both UNSW timelines, while the healthy Wednesday intra-day replay remained an unresolved counterexample.Source: Table 11 · p. 22
  • Policy ordering changed with candidate comparability, and frozen preprocessing and a fourfold evidence disadvantage accounted for different observed harms in the evaluated controls.The ordering-change rule fired for ATC, DoC and the ensemble under exact-feature-disjoint roles; nominal row-count parity does not establish information parity.Source: §6 · p. 22
  • +0.53, +1.67 and +0.38 balanced-accuracy points were gained by raising evidence from 512 to 2,000 samples per class under exact-feature-disjoint progressive drift, with benchmark-dependent effects driven mainly by fewer false positives.Effects were positive and statistically resolved in all three benchmarks, but the ToN-IoT effect was sub-material.Source: §6 · p. 22
  • Validation helped when challenger construction or evidence was asymmetric, but matched-evidence blocks showed no positive resolved gate effect and included one strict-gate cost.The discussion does not support universal validation; on streams with strong incumbent degradation, conservative gates can forfeit recovery.Source: §6 · pp. 22–23
  • No evaluated alternative update policy dominates, and their information, accuracy and update-cost trade-offs apply only to the tested configurations.Under exact-feature-disjoint roles, cost and compatibility findings differed across ATC, the calibrated ensemble, DoC, replay, DDM and ADWIN.Source: §6 · p. 23
  • The full operational stack was not evaluated jointly, and the experiments assume honest candidate data, triggers and validation probes rather than adversarial update manipulation.The stated contribution is evaluation discipline, not a demonstrated or recommended deployment configuration.Source: §6 · p. 23

7 Limitations

The study’s limitations concern benchmark and drift scope, candidate and probe assumptions, learner dependence, and the inferential reach of its controls. Reported harm and benefit patterns should therefore be read conditionally, not as universal properties of adaptive NIDS.

Benchmark and drift scope

  • Three binary public benchmarks do not provide broad external validation; gradual regime-pool mixing is tested, but p(y|x) change and recurrent drift are not isolated.Candidate batches and probes use true current severity; the observed-data arm reproduces harmful-regime rescue, but equivalence to oracle probes and observed-data size controls were not tested.Source: §7 · p. 24

Learner and pipeline scope

  • Full-drift harm is specific to the evaluated SVC-RBF pipeline and does not appear for more robust classifiers; incremental or weighted online learners remain untested.Full-drift absolute false-positive rates are roughly 27–31% on UNSW-Recon and ToN-IoT, and the size control and common-harness comparison used SVC-RBF only.Source: §7 · p. 24

Evidence and duplicate controls

  • Equal nominal per-class sample sizes do not equalize effective information, and exact-feature-disjoint roles address exact duplicates only, not approximate similarity or dependence.With-replacement draws can repeat rows within a role; the positive resolved full-drift size effects are confined to the nested pool design, with material benefit in two of three benchmarks.Source: §7 · p. 24

Joint deployment scope

  • The controls isolate factors separately, so their complete combination and joint deployment behavior remain untested; the proposed operational sequence is a design hypothesis.Mean compatibility at matched size does not rule out an individual committed candidate being worse than the incumbent.Source: §7 · p. 24

Policy comparison scope

  • The common-harness policies use different information budgets, and DDM and ADWIN were evaluated at registered parameters without tuning.The comparison covers fixed policies, not a learned meta-controller; recent systems were not reproduced where their decision units and update semantics differed.Source: §7 · pp. 24–25

Formal and diagnostic scope

  • VBC-SG controls false probe-superiority on the probe distribution under a conditional weak null, not future deployment harm; that bound matches future harm only with a representative probe.Stale probes and coverage results indicate representativeness can fail, and strong within-probe autocorrelation makes the empirical-Bernstein sequence exceed nominal α.Source: §7 · p. 25

Probe and chronological evidence

  • The gate assumes a small labeled probe, but its adjudication count is not an operational inspection-cost estimate; under random inspection its harm-regime protection dissolves at π = 0.01.Thirteen chronological replays show no net harm from always deploying but do not bound harm frequency; ToN-IoT has no timestamps, leaving the controlled harm benchmark without a chronological counterpart.Source: §7 · p. 25

Statistical scope

  • Thirty seeds estimate variability conditional on each benchmark and pool design, not independent deployment environments; external study units are the three benchmarks.The paper emphasizes effect sizes, intervals, benchmark heterogeneity, and sensitivity robustness, with Holm and Benjamini–Hochberg corrections applied to specified families.Source: §7 · p. 25

8 Conclusion

The conclusion is that drift alarms can justify constructing challengers but cannot by themselves justify promotion. Promotion outcomes and policy rankings changed with challenger construction and evidence, so those conditions require explicit control and reporting.

8 Conclusion

  • Under exact-cleaned-feature-disjoint roles and pool-constructed progressive drift, raising evidence from 512 to 2,000 retained positive resolved effects of +0.53, +1.67, and +0.38 balanced-accuracy points.The effects were material in two of three benchmarks and driven mainly by fewer false positives.Source: §8 · p. 25
  • At nominal parity, point and strict validation showed no resolved positive average effect, while strict validation incurred a sub-material cost in one cell.Policy ordering remained candidate-size-dependent, no evaluated policy globally dominated, and earlier ATC and calibrated-ensemble compatibility claims narrowed.Source: §8 · p. 25
  • Thirteen chronological replays showed no net harm from always deploying, but they bound neither its frequency nor its impossibility; the integrated operational stack remains future work.The conclusion calls for challenger construction and evidence to be controlled, reported, and interpreted explicitly when promotion is evaluated.Source: §8 · p. 25

Statements and Declarations

The authors report no specific funding or competing interests. They provide availability and contribution information, and describe their use of AI-assisted tools.

Statements and Declarations

  • The research received no specific grant, and the authors declare no known competing financial interests or personal relationships that could have influenced the work.Ethics approval and consent to participate were not applicable because the study used public benchmarks and involved no human participants or animals; consent for publication was also not applicable.Source: Statements and Declarations · pp. 25–26
  • The source code, protocols, configs, environment specification, reproducibility instructions, result summaries, and hash manifest are archived in the Zenodo artifact.The exact version DOI is 10.5281/zenodo.22239106; public benchmark datasets and raw or generated outputs are not redistributed.Source: Statements and Declarations · p. 26
  • The listed authors’ contributions span conceptualization, methods, software, data curation, analysis, validation, supervision, and writing.Claude and OpenAI Codex assisted with drafting, editing, and analysis-script implementation and review; the authors say they verified the output and take responsibility.Source: Statements and Declarations · p. 26

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