Introduction

Coronary CT angiography (CCTA) supports noninvasive assessment of suspected coronary artery disease [1,2,3]. The Coronary Artery Disease Reporting and Data System (CAD-RADS) standardizes the description of stenosis and related findings [4, 5]. Health-check services can provide linked CCTA, coronary calcium scoring, low-dose computed tomography (LDCT), and clinical records. These records offer an opportunity to study whether routinely collected information predicts CCTA findings.

Noncontrast, noncardiac chest CT contains cardiovascular information beyond its original indication. Consensus statements describe coronary calcium assessment on these examinations [6,7,8], and reviews place it within broader opportunistic CT assessment [9, 10]. Studies of lung cancer screening and LDCT have examined calcium, radiomics, and deep learning predictors of cardiovascular events or coronary disease [11,12,13,14,15,16]. Other studies have assessed whether coronary calcium on routine chest CT helps characterize downstream CCTA findings in selected populations [17, 18]. Together, this work supports evaluating LDCT-derived measurements alongside routine clinical predictors.

Machine learning models combining clinical information and coronary calcium have been evaluated for obstructive coronary disease, while deep learning has been applied to CCTA plaque and stenosis analysis [19, 20]. Combining clinical data sources presents a further problem: laboratory results and medical histories may be missing for entire groups of participants. One approach selects a model using the largest available feature set; another averages predictions from several models compatible with the available data. Comparing these approaches with a selected compatible single model, a common-feature ensemble, and imputation models can distinguish the benefit of aggregation from that of using optional inputs.

We evaluated an ensemble using eight routine clinical and 31 LDCT-derived inputs, with optional laboratory and encoded history blocks. The common feature set was used for every participant, with imputation of missing clinical values. The objective was to determine whether aggregating compatible predictors improved on compatible single models, common-feature models, and imputation-based alternatives under nested internal validation. We assessed discrimination, prediction error, calibration, and exploratory decision thresholds. Reporting was guided by the Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis with Artificial Intelligence (TRIPOD + AI) statement and Checklist for Artificial Intelligence in Medical Imaging (CLAIM) [21, 22]. The Prediction Model Risk of Bias Assessment Tool with Artificial Intelligence (PROBAST + AI) informed consideration of bias and applicability [23].

Materials and Methods

Study Design and Population

This retrospective model-development and internal-validation study used records from a single hospital health-check service in Taiwan. Examinations were determined by clinical care. Records were assembled for the 1 July 2024 to 28 February 2025 collection period. Among 888 participants with extracted LDCT features, 24 had been excluded because their images did not meet study requirements, leaving 864 with an analysis endpoint. The study team confirmed that the records represented different people without repeated examinations under different identifiers. A complete consecutive-enrollment denominator, symptom classification, and individual CCTA indications were unavailable. Figure 1 shows study flow and validation; Table 1 summarizes baseline characteristics.

Fig. 1
Fig. 1
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Study flow and nested validation. Of 888 distinct participants with source records, 864 contributed to modeling and manual QC. Model selection and calibration were confined to outer training data. Predictor availability refers to the retrospective dataset

Table 1 Clinical characteristics by mutually exclusive data-availability group
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Records were linked at participant level. The health-report examination date agreed with the LDCT Digital Imaging and Communications in Medicine (DICOM) study date in 854/864 cases and differed in 10, including one LDCT from 2023. Source-image checks supported the discrepant LDCT dates. Report-header dates could not establish CCTA acquisition dates, so exact LDCT–CCTA intervals remained unknown. The historical image exclusions lacked detailed failure categories, decision dates, and records of blinding to CCTA findings. Manual quality control (QC) of included cases was conducted separately during revision.

The Institutional Review Board of Cheng Hsin General Hospital approved the study (IRB No. (97)237) and waived individual informed consent for retrospective analysis of de-identified data. Identifiers, report-derived CAD-RADS categories, and the outcome were excluded from predictor inputs. The available sample determined study size; no prospective sample-size calculation was undertaken.

The primary endpoint was report-derived CAD-RADS ≥ 3: categories 0–2 were endpoint-negative, and categories 3, 4 A, 4 B, and 5 were endpoint-positive [4, 5]. This measures anatomic CCTA findings. A CAD-RADS ≥ 4 sensitivity analysis used separate model fitting and validation.

Endpoints came from routine clinical reports, without a new consensus rereading. Four identifiable CCTA reporting radiologists accounted for 857 records; seven report sections lacked a recovered signer. Seven established endpoint labels lacked a recovered explicit CAD-RADS category statement; these established labels were retained. Six records belonged to both subsets. Historical reader experience and inter-reader agreement were unavailable. No standalone CAD-RADS N category was present in the analytic endpoint, and no N category or modifier appeared in recovered explicit category lines. Incomplete report text precluded a comprehensive count of nondiagnostic examinations.

Predictor Definitions and Availability

The common feature set contained age, sex, height, weight, body mass index (BMI), systolic and diastolic blood pressure, pulse rate, and 31 LDCT-derived measurements. The laboratory feature set added 16 measurements covering complete blood count, fasting glucose, glycated hemoglobin, renal function, and lipids. The history feature set added 25 encoded fields covering medical and surgical history, family history, medications, smoking, alcohol use, and explicit none/unknown indicators. The combined feature set contained 80 raw inputs before encoding and missingness features. Definitions, observed codes, and completeness are provided in Online Resource 1, Section S1.

Heart, aorta, and five lung-lobe masks were generated using TotalSegmentator [24] in native LDCT geometry. The saved environment record lists TotalSegmentator 2.12.0 and Python 3.12.4; software versions were not recorded separately for each examination. The lung region of interest (ROI) was the union of the five lobes. The heart-centered ROI incorporated 5 mm dilation, slice-wise filling, and convex-hull processing. Feature extraction then restricted this ROI to the lung axial extent, removed lung overlap, and applied 2 mm erosion, largest-component selection, and dilation cleanup. The resulting ROIs sampled regional calcium and fat rather than delineating individual coronary arteries, valves, or the pericardium.

Two reviewers with 7 and 3 years of image-reading experience assessed all 864 analysis cases for coverage and inclusion of nontarget tissue in the heart calcium, aortic/periaortic calcium, and pericardiac ring-fat regions. A third physician served as adjudicator for disagreements. Technical QC assessed file readability, geometry, labels, and nonempty masks in all 888 source cases. An independent Python implementation checked 31 scalar measurements per case against fixed numerical tolerances. Online Resource 1, Section S3 reports the human and technical QC assessments.

Scalar features were originally computed in MATLAB R2025b with the Image Processing Toolbox after conversion to Hounsfield units (HU). Calcium volumes used thresholds of 130, 200, 300, and 400 HU. Heart connected-component descriptors used the 130-HU threshold and excluded clusters smaller than three voxels; total calcium volumes did not apply that cluster exclusion. Periaortic calcium sampled the intersection of a 5 mm aortic dilation and the cleaned heart ROI. Regional calcium proxies used nonnegative differences between ROI measurements and were not formal coronary or Agatston scores. Dedicated clinical calcium scores were not used as proxy predictors. Additional measurements described aortic equivalent diameter and area, lung attenuation, and a 10 mm external heart ring excluding heart, lung, and aorta, with fat defined from − 190 to − 30 HU. Online Resource 1, Section S1 gives the full feature definitions.

The source LDCT acquisition used a 128-slice dual-source scanner (Somatom Definition Flash, Siemens Healthineers, Erlangen, Germany), noncontrast and nongated, during deep-inspiratory breath-hold: 120 kVp, 30 mAs, 0.6 mm collimation, 0.5 s rotation time, and pitch 1.2. Automated voltage/current modulation was not used. Reconstructions used 3 mm slice thickness, filtered back-projection, and a standard-resolution B40 kernel.

Availability was defined by structured information in the retrospective analysis dataset. Four mutually exclusive groups had neither optional block, laboratory data only, history data only, or both blocks. Proxy features were calculated retrospectively. Joint-order, laboratory-release, and questionnaire-entry timestamps and uniform variable-specific look-back windows were unavailable, so predictor availability at CCTA ordering could not be verified.

At least one observed structured predictor within a block reproduced its stored availability flag in the frozen dataset. This describes the existing coding; the original completeness rule could not be recovered. Laboratory data were present in 475 participants: 474 had all 16 measurements and one lacked estimated glomerular filtration rate. The other 389 had no laboratory values. All 25 encoded history fields were populated in 405 participants and absent in 459. Unknown/none codes were retained separately from missing cells. One of 406 recovered questionnaires lacked an encoded analytic history block. The complete historical transformation script was unavailable, so numeric smoking/alcohol codes were retained without assigning new clinical labels.

Learners and Preprocessing

The original pool comprised logistic regression, histogram gradient boosting, random forest, extra trees, gradient boosting, and Gaussian naive Bayes. Four feature sets produced 24 candidate models; models requiring optional blocks were fitted only in eligible training participants. Numeric median imputation and categorical vocabularies were learned within each training subset. Sex and encoded smoking/alcohol status were one-hot encoded, with an explicit missing token and unseen categories ignored. Row-wise missingness indicators and counts were added. Logistic regression and Gaussian naive Bayes also used training-fitted standardization. Online Resource 1, Section S2 specifies class weighting and algorithm settings.

The six-learner hyperparameters and top-3 rule were inherited from earlier development on this dataset and fixed before the nested revision runs. Repeated-split and sensitivity protocols were specified after the primary analysis results were known. These analyses therefore evaluate robustness within a previously explored dataset.

Five outer folds were generated using a fixed random seed (42), with joint stratification by endpoint and availability group. Within each outer training set, five new inner folds generated out-of-fold (OOF) predictions for eligible candidate models. Each inner fit learned its own preprocessing; only inner predictions and outcomes determined model ranking, selection, and weights. Candidates were then refitted on eligible outer training participants and used to predict the outer test participants. Each participant contributed one outer-test prediction per procedure. Saved split membership, fit-input hashes, prediction records, and replay checks verified that outer test labels were excluded from fitting, selection, weighting, and calibration.

Comparator Definitions

The primary comparator selected one model from all candidates compatible with a participant’s availability group, ranked by inner average precision. We refer to this procedure as “compatible single.” The richest-scope router restricted selection to candidates using the largest available feature set. The “common single” procedure selected one model using only the common clinical and LDCT inputs, ranked on pooled inner predictions, and applied it across availability groups.

Global imputation baselines used all training participants and all 80 raw inputs: unweighted L2 logistic regression with and without additional missingness indicators, and single-model selection from an expanded pool. Categorical missing tokens remained in the version without additional indicators. Ensemble controls averaged the same selected three models with equal weights, all compatible models with equal weights, or three common-feature models selected within each availability group. A pooled common-feature top-3 control used the same models and weights across all groups. An availability-only baseline assigned each group its outer-training event fraction.

Adaptive Aggregation and Calibration

For each availability group, compatible candidates were ranked by average precision from inner OOF predictions in that group. With fewer than 10 valid observations or only one outcome class, ranking used pooled eligible inner predictions. Candidates whose scores remained unusable were excluded when valid alternatives existed. Up to three highest-ranked valid candidates received weights proportional to their nonnegative average precision; ties followed a fixed lexical order. If all scores were unusable, the first compatible candidates in that order received equal weights; a nonpositive sum of selected scores also triggered equal weights. Neither equal-weight fallback occurred in the recorded runs. Both this procedure and Super Learner use cross-validation to combine candidate predictors [25], but the present weights were proportional to individual average precision rather than optimized for ensemble loss.

We evaluated both raw probabilities and sigmoid-calibrated probabilities. Within each outer training set, three calibration folds repeated the entire inner selection, refitting, and routing procedure. Each held-out calibration participant was predicted by a procedure fitted without that participant. A logistic calibrator was fitted to the resulting cross-fitted score logits and outcomes, then applied to that outer fold’s test predictions. Each outer fold had a separate calibrator. Although each sigmoid mapping is monotonic, different mappings across folds can change the ranking of pooled OOF predictions. Raw and calibrated results are both reported.

Robustness Analyses

Raw nested validation was repeated across five reproducible random partitions of the same 864 participants; random-number initialization is specified in Online Resource 1, Section S2. A CAD-RADS ≥ 4 analysis rebuilt endpoint-stratified splits and repeated selection, fitting, and calibration for 116 events. An expanded pool added XGBoost and LightGBM with two fixed configurations per family; inner average precision selected one configuration per family and feature set before ranking candidates. The original class weighting was retained; added boosters were unweighted and used no early stopping.

Matched feature analyses compared common and augmented predictors in laboratory-available participants (475; 101 events), history-available participants (405; 111 events), and participants with both blocks (228; 54 events). Each comparison used identical eligible training/test participants and learner-specific seeds, with separate inner model selection for the two feature sets. The first two populations include the third. The pooled common-feature ensemble was added after expanded-pool results were available and was exploratory. A low-calcium subgroup was defined by the outer-training 25th percentile of the heart-region calcium proxy, applied to the corresponding test fold; this differs from an Agatston-zero subgroup. Earlier top-k, random-ensemble, and masked mixture-of-experts experiments [26] are reported separately in Online Resource 1, Section S10.

Evaluation and Statistical Analysis

Evaluation included area under the receiver operating characteristic curve (AUROC), area under the precision–recall curve (AUPRC, estimated as average precision), Brier score, expected calibration error (ECE), and decision-curve net benefit [27,28,29,30]. ECE used 10 equal-width probability bins. Calibration slope and intercept were jointly estimated by logistic regression of outcome on the logit of held-out probability. The joint intercept differs from calibration-in-the-large, which fixes the slope at one. Decision curves used thresholds 0.01–0.50 in steps of 0.01, with a descriptive mean across 0.10–0.20. This band and operating points 0.05, 0.10, 0.15, and 0.20 were exploratory.

Point estimates and paired differences were reported with percentile 95% confidence intervals (CIs) from 2000 participant-level bootstrap resamples. Both procedures used the same participants in each resample. Fixed random-number initialization ensured reproducible resampling; implementation details are provided in Online Resource 1, Section S2. These intervals condition on fixed OOF predictions, incompletely represent fitting and selection uncertainty, and are unadjusted for multiple comparisons. We interpreted them as exploratory estimates, without independent-fold t-tests or converting favorable bootstrap fractions into p-values.

Threshold tables report true and false positives and negatives, the fraction above threshold, and negative predictive value. False-negative proportions use endpoint-positive participants as the denominator, with Wilson 95% intervals for the observed held-out counts. These intervals do not include full model-development uncertainty. Cohort characteristics were summarized descriptively.

Generative AI tools assisted analysis-code development and checking, manuscript drafting, organization, and formatting. Figures were generated from recorded results with plotting code, without generative image synthesis. The authors are responsible for scientific interpretation and final approval.

Results

Participants and Proxy Quality Control

The analysis included 864 participants and 221 CAD-RADS ≥ 3 endpoints (25.6%). Median age among 859 observed ages was 60 years (interquartile range 51–68), and 506 participants were male (58.6%). Availability groups comprised 212 with neither optional block, 247 with laboratory data only, 177 with history data only, and 228 with both, with endpoint prevalences of 29.7%, 19.0%, 32.2%, and 23.7%, respectively (Table 1).

All 888 source CT–mask sets passed the specified readability, geometry, nonempty-mask, and label checks. Independent Python replay reproduced 31 × 888 = 27,528 scalar values within the fixed tolerance, with no missingness mismatch. Human reviewers identified no major defects and considered all 864 analysis cases acceptable for the intended proxy measurements. Online Resource 1, Section S3 provides the QC results.

Nested Prediction Performance

With the original six-learner pool, raw adaptive top-3 achieved AUROC 0.8072, AUPRC 0.6160, and Brier score 0.14389. After calibration, these values were 0.8080, 0.6220, and 0.14152, with ECE 0.0220, calibration slope 1.077, and joint intercept 0.067. Calibrated compatible single achieved AUROC 0.7887, AUPRC 0.5917, Brier score 0.15326, and ECE 0.0672, with slope 1.381 and intercept 0.299. Table 2 reports raw and calibrated estimates; full intervals appear in Online Resource 1, Section S4.

Table 2 Raw and calibrated nested prediction performance with the original six-learner pool
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For calibrated top-3 minus compatible single, ΔAUROC was + 0.0193 (95% CI 0.0029–0.0358), ΔAUPRC + 0.0303 (− 0.0070 to 0.0667), and ΔBrier − 0.01174 (− 0.01723 to − 0.00621). Mean net-benefit difference over 0.10–0.20 was + 0.0091 (− 0.0007 to 0.0181). Relative to calibrated common single, ΔBrier was − 0.00540 (− 0.00981 to − 0.00053), while AUROC and AUPRC intervals crossed zero. Against common-feature top-3 selected within availability groups, ΔBrier was − 0.00005 (− 0.00295 to 0.00306); discrimination and net-benefit intervals also crossed zero. Equal weighting of the same three models produced nearly identical estimates (Table 3; Fig. 2).

Table 3 Calibrated adaptive top-3 minus calibrated comparator with the original six-learner pool
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Fig. 2
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Paired prediction-error comparisons for sigmoid-calibrated procedures. Adaptive top-3 minus the indicated comparator for a the original six-learner pool and b the expanded pool. Negative Brier differences favor top-3. Intervals are conditional paired 95% bootstrap intervals without multiplicity adjustment. The pooled common-feature control in panel b was an exploratory addendum

Figure 3 shows calibration and decision curves; Online Resource 1, Fig. S1 shows discrimination curves. Paired ECE comparisons with the common-feature models had intervals crossing zero. The availability-only baseline achieved AUROC 0.5720, AUPRC 0.2955, and Brier score 0.18776.

Fig. 3
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Calibration and exploratory decision curves. Original-pool sigmoid-calibrated procedures evaluated with one held-out prediction per participant. a Observed event fractions against mean predicted probabilities in 10 equal-width bins; individual-bin counts and Wilson intervals are in the supplementary aggregate tables. b Net benefit versus refer-all and refer-none policies. Shading marks the exploratory 0.10–0.20 threshold band; it is not a recommended referral range

At a risk threshold of 0.15, calibrated top-3 classified 508/864 participants (58.8%) above threshold and missed 29/221 endpoint-positive participants (13.1%; 95% Wilson CI 9.3–18.2%). Those 29 participants represented 3.4% of the cohort. Of the 356 below threshold, 327 were endpoint-negative, giving a negative predictive value of 91.9%. At thresholds 0.10 and 0.20, the missed-positive proportions were 6.8% and 18.6% (Table 4).

Table 4 Exploratory threshold trade-offs for calibrated adaptive top-3
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Expanded Model Pool and Ensemble Controls

In the expanded pool, calibrated top-3 achieved AUROC 0.8079, AUPRC 0.6188, and Brier score 0.14155. Relative to compatible single, differences were + 0.0227 (0.0086–0.0375), + 0.0342 (0.0054–0.0601), and − 0.01258 (− 0.01668 to − 0.00800), respectively. Relative to the expanded-pool global imputation model, ΔAUROC was + 0.0053 (− 0.0139 to 0.0235), ΔAUPRC + 0.0020 (− 0.0282 to 0.0314), and ΔBrier − 0.00382 (− 0.00817 to 0.00119).

Calibrated pooled common-feature top-3 achieved AUROC 0.7995, AUPRC 0.6022, and Brier score 0.14398. Adaptive top-3 differences were + 0.0085 (− 0.0083 to 0.0238), + 0.0166 (− 0.0104 to 0.0428), and − 0.00243 (− 0.00682 to 0.00206), respectively; the net-benefit interval also crossed zero. Selected weights were close to equal, and the equal-weight comparison was inconclusive. Across availability groups, expanded adaptive top-3 required 9–10 distinct fitted models per outer fold, compared with three for pooled common top-3 and one for common single (Online Resource 1, Section S6).

Incremental Laboratory and History Information

In matched training/test populations, laboratory augmentation of the calibrated single-model procedure improved AUROC by + 0.0379 (0.0074–0.0720), AUPRC by + 0.0744 (0.0109–0.1415), and Brier score by − 0.00818 (− 0.01572 to − 0.00158). History-only augmentation did not show a clear increment: ΔAUROC + 0.0008 (− 0.0140 to 0.0143), ΔAUPRC − 0.0013 (− 0.0225 to 0.0198), and ΔBrier + 0.00010 (− 0.00316 to 0.00329). In participants with both blocks, single-model augmentation improved AUROC by + 0.0685 (0.0040–0.1359), but AUPRC and Brier intervals crossed zero.

For matched top-3 procedures, AUROC, AUPRC, and Brier intervals for all three feature increments crossed zero (Fig. 4; Online Resource 1, Section S7). The laboratory-available and history-available populations overlapped in the 228 participants with both blocks.

Fig. 4
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Matched feature increments after calibration. Common and augmented procedures used the same eligible training/test participants. Points compare single-model selection and top-3 selection in laboratory-available (n = 475), history-available (n = 405), and both-available (n = 228) populations. The first two include the third. Positive AUROC and negative Brier differences favor augmented predictors. Intervals are conditional paired 95% bootstrap intervals without multiplicity adjustment

Split Stability and Endpoint Sensitivity

Across five raw nested split seeds, adaptive top-3 mean AUROC was 0.8058 (range 0.7939–0.8140), mean AUPRC 0.6129 (0.5935–0.6261), and mean Brier score 0.14418 (0.14104–0.14795). AUROC and Brier were more favorable than compatible single in all five splits; results relative to common models varied. Common-feature top-3 mean AUROC was 0.8115 and mean Brier score 0.14346. Of 300 model selections across folds and availability groups, 208 used common predictors, 56 laboratory-augmented predictors, 36 history-augmented predictors, and none the combined feature set (Online Resource 1, Section S8 and Fig. S2).

Encoded dimensions ranged from 83 to 171 in the evaluated models. The population eligible for the combined feature set contained 228 participants and 54 events.

For CAD-RADS ≥ 4 (116/864 events), the separately refitted calibrated top-3 procedure achieved AUROC 0.7804, AUPRC 0.3616, and Brier score 0.10121. Relative to compatible single, ΔAUROC was + 0.0430 (0.0129–0.0764) and ΔBrier − 0.00637 (− 0.01032 to − 0.00255). Intervals against common-feature top-3 crossed zero for discrimination, Brier score, and mean net benefit (Online Resource 1, Section S9).

The subgroup below the training-defined calcium-proxy threshold comprised 216 participants with 30 events. Calibrated adaptive top-3 achieved AUROC 0.7104, AUPRC 0.3419, and Brier score 0.11214, compared with 0.7242, 0.3581, and 0.10816 for common-feature top-3. The Brier difference was + 0.00398 (0.00010–0.00848), favoring the common-feature ensemble. Online Resource 1, Section S5 reports this subgroup and the availability groups.

Discussion

After sigmoid calibration in this cohort, averaging three selected compatible models improved AUROC and Brier score relative to selecting one compatible model. The finding persisted in the expanded pool, which also showed an AUPRC improvement for that comparison. The comparisons with expanded-pool global imputation and pooled common-feature ensembles were less conclusive: their difference intervals included zero. Equal weights produced similar estimates to average-precision weights. These results suggest that averaging contributes to performance, while the additional benefit of selecting different ensembles by data availability remains uncertain.

The choice of comparator matters. The richest-scope router restricts selection to the largest available feature set, whereas compatible single can select from any usable feature set. Common-feature ensembles test whether optional inputs add value beyond averaging models with the same inputs. Models using both optional blocks also had fewer eligible training participants and events. Their absence from the selected ensembles could reflect sample size, correlated or redundant inputs, or model specification; it does not identify which combined features are useful.

The performance of common-feature models is consistent with evidence that routine clinical variables and noncardiac chest CT measurements contain information about coronary disease [6,7,8,9,10,11,12,13,14,15,16,17,18,19]. In matched populations, adding laboratory variables improved the selected single-model procedure, while history increments were uncertain. None of the top-3 feature increments had intervals excluding zero. Thus, an optional data source that helps one selected model may add little once several common-feature predictions are averaged. For deployment, the added inputs and 9–10 retained models would need to justify their data-collection and maintenance costs relative to simpler comparators.

Calibration is central to interpreting probabilities at clinical thresholds [29]. Brier score measures overall probability error, while calibration curves, slope, intercept, and ECE describe other aspects of agreement between predictions and outcomes. Some calibrated single-model procedures remained poorly calibrated. At threshold 0.15, 41.2% of participants were below threshold, but this group contained 13.1% of all endpoint-positive participants. These estimates describe a hypothetical trade-off; no acceptable miss rate, change in actual CCTA ordering, or patient benefit was assessed.

The earlier masked mixture-of-experts experiment was not repeated within the nested procedure, so its results apply to that implementation and evaluation. A fair comparison of learned gating with tabular aggregation would require equivalent training and validation. More broadly, clinical implementation requires evaluation of how predictions affect care as well as their statistical performance [31].

CAD-RADS ≥ 3 denotes anatomic findings on completed CCTA rather than the clinical indication for ordering CCTA. Examinations classified as CAD-RADS 0–2 can still inform plaque assessment and preventive care. Trials of anatomic testing and of CCTA before invasive angiography address different decisions from LDCT-based triage [32,33,34,35]. A prospective study must therefore define the intended ordering decision and evaluate consequences beyond the CAD-RADS threshold.

Several limitations affect interpretation. The cohort came from a selected single-center health-check archive, with an incomplete consecutive-enrollment denominator and unavailable symptom and indication data. Local workflow and documentation may explain some availability-group differences. Retrospective predictor extraction, unverified release times, and uncertain LDCT–CCTA intervals limit interpretation at an actual ordering decision. One linked LDCT predated the nominal collection period. Source records were insufficient for a reliable timing sensitivity analysis.

The 24 historical image exclusions lacked detailed categories and blinding records. Endpoints relied on routine reports with some incomplete category and signer information and no reproducibility reread. Human QC addressed suitability of regional proxy measurements, and numerical replay established calculation consistency. Stability across scanners and protocols remains untested, and the original history-code transformation was incompletely recoverable.

The confidence intervals are conditional on fixed OOF predictions. Dependence from overlapping training sets, prior exploration of the dataset, limited configuration searches, multiple comparisons, and small subgroups constrain inference. The five split seeds reuse the same participants and provide stability estimates rather than independent replications. Intervals crossing zero leave both benefit and harm plausible; they do not demonstrate equivalence or noninferiority.

External validation should assess discrimination and calibration across scanners, protocols, referral settings, and data-availability patterns. Prospective evaluation should verify predictor availability at the intended decision and measure missed findings, referral volume, clinician overrides, and downstream management. Common-feature ensembles and imputation models should remain comparators so that the value of additional inputs and routing can be assessed directly.

Conclusion

Among 864 health-check participants, nested evaluation favored compatible top-3 aggregation over compatible single-model selection for AUROC and Brier score. Laboratory variables contributed to selected single models, but comparisons with expanded-pool imputation and common-feature ensembles left the additional value of availability-specific routing uncertain. External and prospective evaluation is needed to establish whether these retrospective findings can improve clinical triage.