This systematic review was conducted and reported in accordance with the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) guidelines [9]. Given the focus on prediction model development and validation, data extraction and synthesis were additionally informed by relevant items from the TRIPOD (Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis) and TRIPOD–Artificial Intelligence (TRIPOD-AI) reporting frameworks to support structured evaluation of model characteristics, validation strategies, and reporting quality [10,11]. This review was not prospectively registered in PROSPERO because protocol registration was not completed before screening had begun; this is acknowledged as a limitation.

Studies were eligible for inclusion if they met the following criteria: (1) involved adult patients (aged ≥18 years) admitted to hospital settings, including ICUs, general medical or surgical wards, or mixed ICU–ward cohorts; (2) developed, validated, or updated multivariable prediction models using routinely collected EHR or administrative data; (3) predicted delirium occurring during the index hospital admission; and (4) reported sufficient methodological or performance information to allow data extraction.

Eligible outcomes included delirium occurring during the index hospital admission, identified using validated clinical assessment tools (eg, CAM and CAM-ICU), diagnostic codes, or structured chart review. Although the search strategy was designed to capture a broader range of acute mental status deterioration outcomes, all studies meeting inclusion criteria at full-text review predicted delirium. Therefore, delirium was treated as the primary outcome for this review.

Studies using any statistical or machine learning–based modeling approach were eligible, including traditional regression-based models and advanced machine learning methods. Both retrospective and prospective study designs were included. Studies were excluded if they (1) focused exclusively on pediatric populations; (2) were conducted in outpatient, community, or psychiatric clinic settings without hospital admission; (3) relied solely on nonroutine data sources such as imaging, genomics, or specialized psychometric instruments not typically available in EHR systems; (4) predicted outcomes defined at the population level or occurring outside the index hospital admission (eg, long-term suicide risk or postdischarge psychiatric readmission); or (5) did not report delirium or an equivalent acute in-hospital mental status outcome.

A comprehensive literature search was conducted to identify studies developing or validating prediction models for delirium and related acute mental status outcomes occurring during hospitalization. The search strategy was designed a priori to be intentionally broad to maximize sensitivity and capture models targeting a range of clinically relevant mental status changes. However, all studies meeting inclusion criteria at full-text review focused exclusively on delirium. This reflects the predominance of delirium as the most consistently defined and operationalized outcome in this field, and the present review therefore focuses specifically on delirium prediction models.

The following electronic databases were searched from inception to November 11, 2025: PubMed or MEDLINE, Embase, PsycINFO, and Web of Science. The search combined terms related to prediction modeling and machine learning (eg, prediction, risk model, machine learning, and AI), routinely collected health care data (eg, EHRs, administrative data, and claims data), acute mental status outcomes (eg, delirium, acute confusion, agitation, mental status change, and psychotropic medication use), and hospital settings (eg, inpatient, ward, and ICU).

Database-specific search strategies were developed using a combination of controlled vocabulary (eg, MeSH) and free-text terms. Full search strategies for each database are provided in Multimedia Appendix 1. No restrictions were placed on geographic location or health care setting. Only studies published in English were included. Reference lists of included studies and relevant review papers were manually screened to identify additional eligible studies. All retrieved records were imported into reference management software, and duplicate records were removed before screening.

After removal of duplicate records, titles and abstracts were screened to identify potentially eligible studies. Full-text papers were retrieved for all records deemed potentially relevant and assessed against the predefined eligibility criteria. Study selection was performed independently by 2 reviewers (CSL and GWC). Discrepancies at either the title or abstract or full-text screening stage were resolved through discussion and consensus, with consultation of a third reviewer (MHT) when necessary. The overall study selection process is summarized using a PRISMA flow diagram.

Data were extracted independently by 2 reviewers (CSL and GWC) using a standardized data extraction form developed a priori. The extraction framework was informed by established guidance for prediction model studies, including the CHARMS (Checklist for Critical Appraisal and Data Extraction for Systematic Reviews of Prediction Modelling Studies), and reporting domains from the TRIPOD and TRIPOD-AI statements [10-12].

For each included study, extracted information included study metadata (first author, year, country, clinical setting, and study design), population characteristics (sample size and cohort definition), outcome definition and ascertainment method (eg, CAM-based assessment, ICD [International Classification of Diseases] codes, and chart review), prediction time horizon, modeling approach, predictor variables, feature selection methods, and model presentation.

Model development and validation characteristics were extracted in detail, including type of validation (internal, temporal, or external), validation datasets, and reported performance measures. Extracted performance metrics included measures of discrimination (eg, area under the receiver operating characteristic curve [AUROC]), sensitivity, specificity, and predictive values where available. Calibration measures and decision-analytic measures (eg, decision curve analysis) were recorded when reported. Information on missing data handling was extracted for each study, including use of complete-case analysis, single or multiple imputation, or algorithm-intrinsic handling of missingness. Where missing data handling was not explicitly described, this was recorded as not reported.

Risk of bias and applicability of included studies were assessed using the PROBAST (Prediction Model Risk of Bias Assessment Tool), which evaluates 4 domains: participants, predictors, outcomes, and analysis [13]. Two reviewers (CSL and GWC) independently completed PROBAST assessments using the tool’s signaling questions. Each domain was rated as low, high, or unclear risk of bias. Discrepancies were resolved through discussion and consensus, with involvement of a third reviewer (MHT) when necessary. PROBAST assessments were used to support qualitative interpretation of methodological strengths and limitations rather than to exclude studies or weight quantitative comparisons.

Given substantial heterogeneity across studies with respect to clinical setting, population characteristics, outcome definitions, prediction horizons, modeling approaches, and validation strategies, a quantitative meta-analysis of model performance was not performed. Findings were therefore synthesized narratively using a structured framework focused on 4 questions: What clinical prediction task was being addressed? What routinely collected data were used? How well models performed under internal and external validation? How close the models were to clinically reliable implementation.

Prediction model characteristics and performance metrics were summarized descriptively. Performance differences were interpreted in relation to clinical setting, prediction horizon, outcome ascertainment, validation strategy, calibration reporting, and risk of bias rather than by algorithm type alone. This approach was chosen to distinguish technical feasibility from clinical readiness.

The database search identified a total of 1086 records, including 274 from PubMed, 373 from Embase, 284 from Web of Science, and 155 from PsycINFO. After removal of duplicate and overlapping records, 673 unique records remained for title and abstract screening, of which 603 were excluded. Seventy reports were retrieved for full-text assessment. Following full-text review, 41 reports were excluded. The most common reasons for exclusion were the absence of a multivariable prediction model, outcomes not occurring during the index hospital admission, wrong publication type, wrong outcome definition, or an ineligible study population. A total of 29 studies met the inclusion criteria and were included in the final qualitative synthesis. The study selection process is summarized in Figure 1.

The 29 included studies did not represent a single uniform prediction problem. Instead, they formed a heterogeneous evidence base spanning early admission screening, perioperative risk prediction, short-term ICU warning systems, and external validation or prospective evaluation of existing tools. Country, center structure, and study design are summarized in Table 1. The narrative synthesis highlights the patterns most relevant to interpretation.

Most studies used retrospective cohort designs (20/29, 69%) [14-23,25,29-33,35,39,40,42]. Of 29 studies, prospective cohorts were less common (4/29, 14%) [26,28,36,37], 4 (14%) studies combined retrospective development with prospective validation or evaluation [27,34,38,41], and 1 (3%) study used a retrospective case-control design [24].

This design profile is important because much of the literature remains closer to model development than to implementation science. The strongest clinical evidence generally came from studies that moved beyond internal validation into external, temporal, or prospective evaluation.

Clinical setting, population focus, and sample size are summarized in Table 2. Clinical settings were unevenly represented. Of 29 studies, general ward populations accounted for 13 (45%) studies, mixed ward-ICU cohorts accounted for 8 (28%), ICU-only cohorts accounted for 7 (24%), and the emergency department accounted for 1 (3%). Fifteen (52%) studies were single-center, while 14 (48%) studies used multicenter data or combined multicenter development with external validation.

Across all studies, adult inpatients constituted the primary population of interest, but the intended use cases differed. Some models were designed for broad hospital screening, some for older adult or surgical pathways, and others for high-frequency monitoring in intensive care. Sample sizes ranged from fewer than 100 patients in a small prospective deployment cohort [27] to more than 100,000 patients in large multidatabase studies [19], making direct comparison of performance estimates difficult.

Outcome definitions, assessment methods, and prevalence are summarized in Table 3. Delirium was the outcome across all included studies, but the clinical meaning of the outcome varied. Of the 29 studies, 27 (93%) modeled incident delirium, 1 (3%) modeled prevalent delirium in the emergency department [15], and 1 (3%) considered any delirium regardless of timing [38]. Outcome labels included in-hospital delirium, postoperative delirium, ICU delirium, and recurrent or short-term delirium risk.

Outcome ascertainment was a major source of heterogeneity. Studies used structured tools such as CAM, CAM-ICU, the Delirium Observation Screening Scale, or the Intensive Care Delirium Screening Checklist, as well as ICD codes, EHR-derived definitions, NLP-enhanced ascertainment, and manual chart review or adjudication. These approaches identify overlapping but not identical clinical events, which limits the interpretability of pooled performance comparisons.

Outcome prevalence also varied substantially. Among the 20 studies with clearly extractable prevalence percentages, 6 (30%) reported prevalence below 5%, 10 (50%) reported prevalence between 5% and 20%, and 4 (20%) reported prevalence above 20%. Low prevalence was typical in general ward and broad inpatient cohorts, whereas higher prevalence was more common in ICU, surgical, and selected high-risk cohorts.

This variation has direct implications for clinical interpretation. In low-prevalence settings, even a model with good AUROC may have low positive predictive value (PPV) and may generate many false-positive alerts. In higher-prevalence settings, the same threshold can produce a very different balance between missed cases and unnecessary intervention.

Prediction horizon and TRIPOD classification are summarized in Table 4. Prediction horizons further separated the studies into different clinical tasks. Some models estimated risk at admission or during the first 24‐72 hours, some predicted postoperative delirium over a fixed perioperative period, and others updated risk dynamically using rolling ICU or hospital windows. These are not interchangeable tasks: short-term dynamic prediction benefits from more proximal clinical signals, whereas admission-time models must support earlier but less certain prevention decisions.

Accordingly, apparent differences in discrimination should not be interpreted as simple evidence that one model family is superior. They may instead reflect differences in timing, population acuity, outcome prevalence, and availability of predictors close to delirium onset.

TRIPOD classifications also reflected a field still weighted toward development and validation rather than deployment. Type 1b and 2b studies predominated, while fewer studies focused on external validation, model updating, temporal validation, or prospective implementation.

Taken together, the study characteristics show that the literature is clinically broad but methodologically fragmented. The central synthesis question is therefore not only whether EHR-based delirium prediction is feasible but which models have been tested under conditions close enough to their intended clinical use.

Model categories are summarized in Table 5, with detailed model development and predictor characteristics provided in Multimedia Appendix 2 [14-42]. Machine learning models were the largest single group (10/29, 34%), followed by statistical or rule-based approaches (8/29, 28%), deep learning models (5/29, 17%), and hybrid approaches combining statistical, machine learning, or deep learning components (6/29, 21%). Tree-based ensemble methods such as random forests and gradient boosting were common, while deep learning was concentrated in ICU or large-scale EHR datasets.

Several studies compared multiple modeling paradigms within the same dataset [16,17,20,22,24,25,31,33,42]. These comparisons did not show a consistent advantage for increasing model complexity. In some cohorts, tree-based or penalized regression models performed similarly to neural network approaches, and apparent internal advantages were not always preserved during external validation.

Predictor sets were built mainly from structured EHR data. Of 29 studies, demographics were included in 28 (97%), comorbidities or diagnostic history in 25 (86%) , laboratory values in 22 (76%), medications in 20 (69%), vital signs in 17 (59%), and nursing or care process variables in 7 (24%). This pattern indicates that most models relied on broadly available routine data rather than specialized research measurements.

Temporal handling of predictors was a key distinction between models (Table 6). Of 29 studies, 15 (52%) used static single-time snapshots, most often at admission, preoperatively, or within an early fixed window. Of 29 studies, 14 (48%) incorporated time-varying information through repeated recalculation, aggregated temporal summaries, rolling windows, or sequential time series modeling.

Of 29 studies, only 8 (28%) used NLP or unstructured free-text data [17,18,23,26,29,38,40,41]. In several of these, NLP supported outcome ascertainment rather than contributing predictor features. Thus, despite the clinical importance of narrative documentation for cognitive and behavioral change, most models remained dependent on structured EHR fields.

Reporting of missing data handling, class imbalance, and interpretability was uneven (Table 7). Missing data handling was not reported in 24% (7/29) of the studies, and class imbalance handling was absent or not reported in 55% (16/29) of the studies. Interpretability was addressed most often through post hoc feature attribution (14/29, 48%) or intrinsically interpretable models (7/29, 24%), but these explanations were rarely linked to clinical workflow decisions.

Overall, model development methods show that EHR-based delirium prediction is technically feasible, but the clinical value of additional data complexity remains uncertain without stronger validation, calibration, and implementation testing.

Model discrimination is summarized in Table 8, with additional model performance metrics, including sensitivity, specificity, PPV, negative predictive value (NPV), and threshold definitions provided in Multimedia Appendix 3 [14-42]. Reported discrimination suggested promising technical performance but should be interpreted cautiously. Of 29 studies, internal AUROC was reported in 24 (83%) studies, with values ranging from 0.77 [24] to 0.97 [23]. Confidence intervals were inconsistently reported, and the internal estimates came from heterogeneous designs, including split-sample validation, cross-validation, temporal evaluation, and prospective cohorts.

Of 29 studies, external AUROC was reported in 12 (41%) studies [15,17,19,24,25,27,29,33,34,37,38,40]. Values ranged from 0.69 in prospective validation [38] to approximately 0.95 in large multisite evaluations [40]. However, external validation datasets differed substantially in clinical setting, prevalence, and outcome definition, limiting direct ranking of models.

Precision-recall performance and threshold reporting are summarized in Table 9. Precision-recall performance was much less frequently reported than AUROC. Of 29 studies, internal precision–recall area under the curve (PR-AUC) was reported in 6 (21%) studies [19-21,30,32,39], and external PR-AUC in 2 (7%) [19,33] studies. This is an important gap because many delirium prediction settings are low-prevalence tasks where AUROC can appear favorable despite limited PPV.

Threshold-based metrics were difficult to compare. Although sensitivity, specificity, PPV, and NPV were often reported, thresholds were selected using different strategies, including data-driven optimization, fixed probability thresholds, and percentile-based risk strata. Few studies justified thresholds in relation to clinical resources, alert burden, or the intended intervention.

The performance synthesis therefore supports a cautious conclusion: routinely collected EHR data can discriminate delirium risk, but discrimination alone does not establish clinical usefulness. For deployment, external calibration, threshold consequences, and decision-analytic benefit are as important as AUROC.

Validation strategies are summarized in Table 10 and show a clear gap between model development and transportability testing. Of 29 studies, 9 (31%) reported internal validation only, 8 (28%) combined internal and external validation, 2 (7%) focused on external validation only, and 2 (7%) reported temporal validation only. Of 29 studies, 3 (10%) were prospective evaluations without a distinct internal or external validation phase; 2 (7%) combined external validation with prospective evaluation; 2 (7%) combined internal, external, and prospective evaluation; and 1 (3%) reported apparent performance only.

Overall, 16 studies reported some form of external or prospective validation [14,15,17,19,23-25,27-29,33,34,37,38,40,41]. Most external validation tested transfer across hospitals, health systems, time periods, or critical care databases. Cross-setting validation, such as applying an ICU-derived model to ward patients or vice versa, was uncommon.

Among the 7 studies with directly comparable internal and external AUROC values, 5 (71%) showed lower discrimination after external validation (Figure 2). The magnitude of decline varied, indicating that performance transportability was influenced by differences in population, data capture, outcome ascertainment, and workflow context.

In this subset, mean internal AUROC was 0.845 and mean external AUROC was 0.772, corresponding to a mean change of −0.073. This descriptive comparison should not be interpreted as a pooled effect estimate, but it illustrates the risk of relying on internal performance when judging deployment readiness.

The external validation evidence was therefore mixed: several models remained discriminative outside their development data, but validation was often conducted in settings similar to the development environment. Evidence for robust transport across substantially different institutions, care pathways, and outcome assessment practices remains limited.

Calibration methods and decision curve analysis are summarized in Table 11. Of 29 studies, calibration was assessed in 15 (52%) studies [15-17,21,24-28,30,32,33,36,37,41]. Methods included calibration plots, Brier scores, Hosmer-Lemeshow tests, calibration slope or calibration-in-the-large, Platt scaling, isotonic regression, and expected calibration error. The diversity of methods, combined with incomplete reporting, made calibration difficult to compare across studies.

Calibration reporting was often less mature than discrimination reporting. Several studies relied mainly on visual assessment, and recalibration after external validation was rare. Of 29 studies, decision curve analysis was reported in only 3 (10%) [17,25,41], leaving limited evidence about whether model-guided decisions would improve net clinical benefit.

Prospective evaluation and implementation characteristics are summarized in Table 12. Of 29 studies, 8 (28%) included prospective evaluation [26-28,34,36-38,41], and 9 (31%) reported some form of workflow integration or implementation testing [26-28,34,36-38,40,41]. These ranged from silent prospective validation to live EHR alerts, but few assessed downstream effects on clinician behavior, prevention delivery, alert burden, or patient outcomes.

Risk of bias was assessed using PROBAST, with domain-level judgments summarized in Multimedia Appendix 4 [14-42] and overall proportions illustrated in Figure 3. Of 29 studies, overall risk of bias was judged low in 8 (28%), unclear in 10 (34%), and high in 11 (38%). The main pattern was not a lack of clinical relevance but limited methodological assurance.

Low-risk studies generally had clearer participant selection, predictor timing, outcome ascertainment, and model evaluation [15,16,21,25,32,33,36,39]. These studies provide the most reliable evidence that routinely collected data can support delirium prediction.

Studies with unclear risk of bias were usually limited by incomplete reporting rather than obvious methodological failure [17,20,22,23,29-31,35,37,42]. Common sources of uncertainty included missing data handling, calibration assessment, feature selection, and validation procedures.

High risk of bias was identified in 11 studies, most often because of analysis-domain limitations [14,18,19,24,26-28,34,38,40,41]. Recurrent issues included apparent-only performance reporting, case-control designs, inadequate handling or reporting of missing data, limited calibration assessment, and incomplete reporting of feature selection.

Within the 11 high-risk studies, inadequate handling or reporting of missing data was identified in 6 studies [26-28,34,38,41], limited or absent calibration assessment in 4 studies [14,19,34,38], apparent-only performance without validation in 1 study [18], case-control design in 2 studies [24,40], and incomplete feature selection reporting in 2 studies [14,19]. Several studies had more than 1 limitation.

These risk-of-bias findings help explain why high AUROC values should not be interpreted as readiness for practice. Models can appear accurate in development datasets while still being vulnerable to overfitting, miscalibration, missing data artifacts, or poor transportability.

Applicability concerns were more limited than risk-of-bias concerns. Most studies evaluated adult inpatient populations and used routinely collected EHR predictors, supporting broad relevance to hospital practice. However, applicability was still context-dependent for ICU-only, perioperative, emergency department, rehabilitation, COVID-19, and single health system models.

The overall quality assessment therefore supports a nuanced interpretation: the field is clinically relevant and technically active, but the evidence base is not yet consistently strong enough to support unqualified clinical deployment. No study was excluded on the basis of PROBAST assessment. Instead, risk-of-bias judgments were used to interpret how much confidence should be placed in the reported performance and implementation claims.

This systematic review included 29 studies developing, validating, or evaluating prediction models for in-hospital delirium using routinely collected EHR data. The principal finding is that EHR-based delirium prediction is feasible across several hospital settings, but the current evidence is fragmented across different clinical prediction tasks. The literature supports the existence of measurable risk signals in routine data; it does not yet establish that any model class is consistently ready for routine clinical deployment.

Four findings are especially important for readers. First, most models were developed retrospectively, and only a minority underwent prospective evaluation or workflow testing. Second, model performance was commonly summarized by AUROC, while calibration, precision-recall metrics, and decision-analytic evaluation were less consistently reported. Third, increased algorithmic complexity did not consistently translate into better or more transportable performance. Fourth, risk of bias was mainly driven by analysis-domain limitations rather than by lack of clinical relevance.

These findings indicate that the next stage of the field should be less focused on producing additional internally validated models and more focused on defining clinical use cases, testing transportability, calibrating models for local populations, and evaluating whether model-guided care changes decisions or outcomes.

The heterogeneity observed in this review is consistent with previous systematic reviews of delirium prediction and broader clinical prediction modeling research [6-8]. Models differed not only in algorithm type but also in clinical setting, prediction timing, outcome ascertainment, and validation design. These differences mean that a single pooled estimate of performance would be difficult to interpret and could obscure clinically meaningful distinctions between prediction tasks.

The predominance of machine learning approaches also mirrors wider trends in hospital and critical care prediction research [43]. However, this review suggests that algorithmic sophistication is not the main bottleneck. In several studies, simpler statistical or tree-based approaches performed similarly to deep learning models, especially when evaluated under comparable conditions. Data quality, predictor timing, outcome definition, and validation context appeared at least as important as model family.

The risk-of-bias patterns also align with metaresearch showing that many published prediction models have limitations in the analysis domain, including missing data handling, overfitting, and incomplete calibration assessment [44]. Evidence that high-risk models often perform less well in external validation [45] is directly relevant here, because several delirium models showed lower discrimination when tested beyond their development data.

Clinically, delirium prediction models are attractive because they could help target prevention, screening, and staffing resources to patients most likely to benefit. The reviewed studies show that routine EHR data contain useful risk information in ward, ICU, perioperative, and emergency care contexts. This supports continued development of delirium prediction as a component of clinical decision support.

The implementation evidence, however, remains incomplete. Few studies assessed whether predictions changed clinician behavior, reduced delirium incidence, improved patient outcomes, or avoided alert fatigue. Without these evaluations, models with favorable discrimination may still have limited value in practice, particularly if thresholds are poorly calibrated to local prevalence and available resources.

Several findings have direct implications for deployment. A model should not be implemented solely because it has a high AUROC. It should have an explicitly defined clinical role, evidence of calibration in the target population, threshold analyses tied to available resources, and prospective evaluation showing that predictions can be acted on without excessive alert burden.

Implementation studies should therefore evaluate not only model performance but also workflow fit, clinician response, alert fatigue, equity, prevention delivery, and patient outcomes. This is particularly important for delirium, where prediction is useful only if it leads to timely and feasible prevention or treatment.

Several limitations should be considered when interpreting the findings of this review. First, the quality of the included evidence base was variable, with a substantial proportion of studies judged to be at high risk of bias, primarily due to analytical limitations. Second, external validation and prospective evaluation were inconsistently performed, limiting confidence in the generalizability of reported performance.

This review also has inherent limitations. Only English-language studies were included, which may introduce language bias. The review was not prospectively registered before screening began, which may increase the risk of reporting bias. In addition, substantial heterogeneity in study design, outcome definitions, and reporting precluded formal meta-analysis. Finally, risk-of-bias assessment relied on the completeness of reporting in the original studies, which may have resulted in conservative or unclear judgments in some cases.

Future research should move from model development toward clinically anchored validation and evaluation. The immediate priority is external and temporal validation across heterogeneous populations, with calibration assessed in ways that can support local recalibration rather than only discrimination ranking.

Implementation research should then test whether predictions change care in practice. Studies should specify the intended intervention pathway, alert threshold, resource assumptions, and monitoring plan before deployment, and should measure clinician response, alert burden, prevention delivery, equity, resource use, and patient outcomes.

Reporting should make threshold consequences easy to interpret. Future studies should present the number of patients flagged, false positives, false negatives, and expected workload at clinically plausible operating points so that health systems can judge whether a model is compatible with local capacity.

Future models may benefit from combining structured EHR variables with unstructured clinical notes, because cognitive and behavioral changes are often documented narratively. NLP-enhanced models should distinguish outcome ascertainment from predictor use, and maintain temporal separation between predictors and outcomes to avoid information leakage.

Expansion beyond delirium to broader acute mental status deterioration may be valuable only when outcomes are clearly defined, temporally valid, and clinically actionable. Across all future work, transparent reporting and alignment with TRIPOD, TRIPOD-AI, CHARMS, and PROBAST will be essential to move from technically promising models toward reliable decision-support tools.

Routinely collected EHR data can support delirium prediction across hospital settings, but favorable discrimination alone does not establish clinical readiness. The evidence remains heterogeneous in outcome definition, prediction timing, prevalence, validation strategy, calibration reporting, and implementation maturity; risk of bias, particularly in the analysis domain, also remains common. More complex algorithms did not consistently improve performance. Future work should prioritize externally validated, well-calibrated, and clinically interpretable models evaluated prospectively within real workflows, with explicit attention to threshold consequences, alert burden, and patient benefit.