In accordance with the PRISMA-ScR reporting checklist and the updated methodological guidance from the Joanna Briggs Institute [29,30], this scoping review defined the scope, characteristics, stages of translation, and gaps for implementation of the clinician-oriented AI-CDSS literature (Supplementary File 1). The objective was to perform descriptive mapping of the evidence instead of conducting pooled effect size or intervention effectiveness evaluation.

The review addressed: (1) the clinical applications and decisions supported; (2) specialties, settings, populations, users, AI methods, and input modalities; (3) evaluation and validation approaches; (4) technical and workflow integration; and (5) adoption, usability, clinical impact, safety, fairness, explainability, economics, privacy, governance, and postimplementation monitoring.

Eligibility criteria were defined using the Population–Concept–Context framework. Population was defined as a set of clinicians, health care professionals, or multidisciplinary teams that had access to information produced by the AI, understood it, and was capable of acting on it for a clinical decision. Concept represented data-based techniques including machine learning, deep learning, natural language processing, large language models, computer vision, reinforcement learning, fuzzy systems, and Bayesian methods, which are used to create information useful for diagnosis, prognosis, risk assessment, treatment, prescribing, triaging, monitoring, alerting, referring, reporting, and workflow decisions. Context included actual health care data or workflow data. The clinical decision-making process or potential integration into workflow were not enough for inclusion.

Studies based on primary empirical reports were only considered to be eligible if the full text exhibited an element of AI, real-life human health care data, and a concrete clinician-facing component that could be useful for patient care decision-making. Studies on model development and validation were not automatically considered to be eligible based on the fact that they used clinical data, had external or temporal validation, compared AI models with the clinicians, and their future possible integration. Tools or outputs with a concrete layer that had not been tested in real-life users or workflows were considered to be Clinical validation. The reports were designated as Prospective/user evaluation if clinicians used or evaluated the AI in a prospective, reader, simulated-workflow, and user-task setting without evaluation of the effect of its usage in live-care; Implementation/impact evaluation if live workflow usage, integration, adoption, operational outcome, patient outcome, or implementation impact were being studied. F5 was the exclusion criterion if a model development/validation lacked a concrete clinician-facing layer.

Source corpus extraction was conducted in PubMed/MEDLINE and was seen as a design boundary as opposed to an affirmation of comprehensive multidisciplinary coverage. A query was conducted in the database on 15 June 2026 based on identical concept syntax per year, beginning from 1 January 2020 to the search date without any language filter used. The start date of 1 January 2020 was kept as a practical boundary for our contemporary times and was reflected retrospectively in the protocol amendment record. Dates, year limits, and output are available in Supplementary File 2. Other data characteristics are available as Tables S1–S5 in Supplementary File 3 and data is given in Supplementary File 4. The annual PubMed/MEDLINE exports contained 14,111 raw records in total. There were no surveillance post-cutoff records included.

Records were managed reproducibly in Python (Supplementary File 5). Duplicate removal occurred in two documented stages: 14 within-year exact-title duplicates and 14 cross-year duplicates after annual concatenation, yielding 14,083 unique screened records. PMID, normalized DOI, and exact normalized title were used; fuzzy matching was not used.

Title/abstract prescreening involved the use of transparent, rule-based approaches in combination with AI-generated recommendations, followed by an assessment by the authors (Supplementary File 6). The rules were designed to prioritize sensitivity by retaining records when the title or abstract did not provide sufficient grounds for exclusion. This design objective does not establish corpus-wide screening sensitivity. The AI recommendations were only for reference purposes and did not define eligibility criteria. The entire corpus was not screened by two humans independently. The prespecified TA200 and FT150 quality control samples were assessed independently by Ali Olamat.

After applying the filters of title/abstract and metadata screens, there were a total of 5140 reports sought for full-text retrieval (Supplementary File 7). For those for which PMC XML was available, it was used. The others not in PMC were searched for through legal means of open access, the publishers’ websites, library databases, or PDF files stored locally. A systematic effort at retrieving reports that could not be found through an interlibrary loan or direct contact with authors was not done for all the reports found to be unavailable. The retrieval summary recorded 1373 of 1449 outside-PMC reports (94.8%) as not retrieved and all 3691 PMC records as assessed. A candidate-level metadata comparison between retrieved and non-retrieved reports was not available.

An identifier-integrity audit found that a prior PubMed-to-PMC mapping process could assign a PMCID that was not an article-level identifier. The mapping was rebuilt using only PubMedData/ArticleIdList identifiers, removing 207 incorrect PMCIDs and yielding 3691 verified PMC candidates plus 1449 outside-PMC candidates. Each acquired PMC XML article was verified against its PMID, DOI, and PMCID.

The eligibility-assessment set comprised 3767 reports, recorded as 3691 PMC XML articles and 76 outside-PMC reports. The same eligibility rules were applied to both sources. A total of 1181 reports were included and 2586 were not included. Included reports were classified as Clinical validation, Prospective/user evaluation, or Implementation/impact evaluation. The 1373 records assigned to the not-retrieved category were recorded separately. Recorded decisions and supporting documentation are provided in Supplementary File 8; Table 1 clarifies the distinction between non-inclusion and a definitive Exclude decision.

The process of full-text processing involved the use of structured extraction, artificial intelligence (AI)-assisted coding assistance, targeted auditing, and human adjudication. The machine-produced results focused on the identification of priority for records or suggestions for code assignment but not in the final decision on eligibility or charting. Targeted human review covered 666 risk-flagged records. Documented remediation activities included consensus resolution of the 152-record disagreement workbook, reconciliation of 24 FT150 disagreements, and targeted integrity re-verification of 90 provisional new inclusions.

A master charting dataset from internal sources that contains 117 variables was used to aid the extraction and validation process. The released public dataset contains 66 variables at the level of reports out of a total of 1181 reports used in this study. Supplementary Data S1 (Supplementary File 4) presents a provenance matrix that captures, for each public variable, the derivation pathway, source variable, basis for verification, scope of dual review, reliability tier, denominator source, and maximum allowable interpretation. This matrix clearly shows that a corpus-wide dual review process was not carried out; DX120 and targeted correction provide bounded validation but not source verification. Study_Design analysis was carried out independent of the final Evaluation_Stage taxonomy and there are 170 Study_Design entries missing.

With a predefined seed of 20260730, Ali Olamat individually scored 200 title/abstracts and 150 full texts using blinded pre-consensus workbooks. These are comparator-specific quality control modules rather than a complete dual-human review of the entire corpus. For DX120, Pınar Özel and Ali Olamat independently completed the core fields in 120 publications; Ali Olamat served as the independent second reviewer. The public package includes deidentified pairs and reproducible metrics; named raw reviewer workbooks and signed author approvals are retained in the restricted/source-lock archive.

Percent exact agreement and Cohen’s κ, Gwet’s AC1, class-specific sensitivity, specificity, precision, negative predictive value, and F1 score were calculated. Confidence intervals of 95% were computed using 2000 bootstrap samples based on the seed 20260809. TA200, FT150, and DX120 interval sampling was achieved by bootstrapping publication records; for DX120, the pooled intervals are obtained through cluster bootstrap by Final_DX_Slot to ensure all the fields from the chosen record are included. TA200, FT150, and DX120 were used as fixed quality control modules rather than sample sizes computed via statistical power analysis. Metrics relative to the final FT150 reference are post-adjudication concordance estimates because the reference contains consensus resolution.

Descriptive analyses were performed based on the report level (N = 1181). The Evaluation_Stage taxonomy used in the final analysis includes Clinical validation, Prospective/user evaluation, and Implementation/impact evaluation. Study_Design was evaluated separately as a multi-coded, source-derived category. Minimal identification/title-based linking revealed 1181 reports in relation to 1180 potential report families. It should be noted that linking was not meant as an attempt to reconstruct the report families in a systematic way and is presented only as a lower-bound duplicate report sensitivity estimate.

For missing-data and absence-detection handling, NR denoted information not reported or not captured and was not interpreted as No. Analysis-ready three-state fields distinguished Detected, Not detected in available extraction, and NR or uncaptured. A not-detected signal was treated as an extraction result rather than proof of absence in the original report. Where a positive source field conflicted with a rule-derived absence flag, the positive field took precedence.

Consistent with the evidence-mapping purpose, no formal report-level risk-of-bias or critical-appraisal tool was applied. Evidence maturity was described through evaluation stage, validation type, prospective or user evaluation, workflow integration, patient or clinical outcomes, calibration, decision-curve analysis, safety, fairness, explainability, economics, and governance or postimplementation evaluation.

No prospective registration occurred for the review. A retrospective protocol, dated 16 August 2026, describes the clinical eligibility criteria, quality control modules, the replacement protocol, the phases of consensus and remediation, the duplicate concordance, the corrections made to the publicly available dataset, the search cutoff date of 15 June 2026, and the resulting corpus of N = 1181 records. A dated explanation, provided on 18 August 2026, provides the justification for the start date of 2020 and the final bootstrap-uncertainty methodology; no changes were made to either eligibility or PRISMA counts.

There were 14,111 raw records across the annual PubMed/MEDLINE exports. In total, 14 within-year duplicates were eliminated before annual canonicalization, which resulted in 14,097 records; moreover, after concatenation, 14 cross-year duplicates were discarded, leaving 14,083 records for screening. A total of 8504 records were excluded during title/abstract screening, and 439 records were excluded during metadata screening. Of 5140 reports sought, 1373 were recorded as not retrieved and 3767 were considered for eligibility. The retrieval summary recorded 1373/1449 outside-PMC candidates (94.8%) as not retrieved and all 3691 verified PMC candidates as assessed. A total of 2586 reports were not included and 1181 reports were included. A summary of validation point estimates is provided in Supplementary File 9 and the complete included-report bibliography is provided in Supplementary File 10. Recorded F1–F10 counts were F1 = 56, F2 = 729, F3 = 194, F4 = 151, F5 = 1120, F6 = 42, F7 = 12, F8 = 11, F9 = 267, and F10 = 4. The final corpus comprised 1137 PMC and 44 outside-PMC reports (Table 1; Figure 1).

No formal risk-of-bias assessment was performed. Descriptive maturity indicators are reported in the main tables and Supplementary Data S1. The public source-level charting dataset contains all 1181 final included publication reports and 66 variables covering bibliographic data, final class, clinical scope, AI approach, input modality, application, evaluation and validation features, integration variables, outcome domains, implementation-gap indicators, and analysis-ready three-state fields.

Publication volume rose markedly after 2024, with 654 of 1181 included reports published in 2025–2026. Country or region terms were captured for 1057 reports. China, the United States, and the United Kingdom were most frequently detected; 249 reports were multicountry and 124 were NR or uncaptured (Figure 2; Supplementary Figure S2 (Supplementary File 7); Supplementary Tables S1 and S2).

The specialties that were coded as the most frequent were oncology and surgery/perioperative care, followed by endocrinology, pulmonology, nephrology, critical care and cardiology. Nephrology was coded in 207 reports (17.5%). Surgery/perioperative specialty was coded in 350 reports (29.6%), whereas an operating-room/perioperative setting was captured in 66 reports (5.6%). The healthcare setting was not mentioned or captured in 702 publications; out of those mentioned, the most common settings were intensive care units and emergency rooms. Lexemes that were associated the most with users were clinicians, physicians, specialists, care team, nurses, and radiologists. The term clinical decision support was kept separate from the professional role as a use-layer signal. Multi-coding was common in signals and many were based on rule-derived coding rather than manually assigned intended user information (Supplementary Table S3).

At least one user-related lexical signal was captured in 1162/1181 (98.4%) reports. The most frequent signals were clinician (962/1181 [81.5%]), physician (695/1181 [58.8%]), specialist (305/1181 [25.8%]), care team (244/1181 [20.7%]), nurse (163/1181 [13.8%]), and radiologist (149/1181 [12.6%]). A separate clinical decision-support use-layer signal was detected in 660/1181 (55.9%) reports. These nonexclusive text-detection counts should not be interpreted as a validated taxonomy of intended users without source-level confirmation (Supplementary Table S3).

Machine learning algorithms that can be used in generic cases including gradient boosting, random forest, deep learning, support vector machines, and large language models or generative AI were the most common types of methods. More than one type of method was found in 733 studies. Structured EHR/EMR and medical imaging were the top two types of inputs, while there were 509 papers where no input type was identified. Multiple types of input were coded in 256 studies (Figure 3, Table 2, Supplementary Figure S5).

Diagnosis/Detection and Prognosis/Risk Prediction took primacy in this area, followed by Screening/Referral, Monitoring, Triage/Prioritization, and Treatment Recommendation/Planning. “Diagnosis/Detection” was encoded in 774 studies and “Prognosis/Risk Prediction” in 588; lack of application information was found in 86. The output categories “Risk/Probability” and “Diagnosis/Classification” were the most common ones. Since applications were multi-coded and mostly rule-derived, they should be treated as evidence map markers but not mutually exclusive functions (Table 2; Figure 4; Supplementary Figure S4).

Final translational stages were Clinical validation (741/1181 [62.7%]), Prospective/user evaluation (270/1181 [22.9%]), and Implementation/impact evaluation (170/1181 [14.4%]). Study-design information was populated in 1011/1181 (85.6%) reports. The most frequent multi-coded design categories were retrospective internal validation (704), external validation (433), prospective clinical evaluation (363), multicenter validation (259), qualitative/mixed methods (116), and usability/human-factors evaluation (109); 170 reports were NR or uncaptured (Table 3; Figure 5).

The internal validation was described in 707 papers, while external validation was mentioned in 441 papers, multicenter validation in 312 papers, and temporal validation in only 27 papers. The prospective assessment and reader/user evaluation were stated in 387 and 323 papers, respectively. The most often mentioned performance domains were discrimination and sensitivity/specificity. Calibration and decision-curve analysis were found in 367 and 277 papers, correspondingly.

A workflow signal was created and characterized for clinicians. As the specific domain for technical integration only showed moderate reliability, it is not included in the main body of the report and is available exclusively in the Supplementary Data S1 and Supplementary File 9.

Adoption/use outcomes were detected in 422 reports and usability/human-factors outcomes in 184. The combined workflow/adoption/usability status was positive in 506, not detected in 584, and NR or uncaptured in 91 reports (Table 4).

Extraction of clinical/patient-outcome information showed very low inter-reviewer reliability in this review. Therefore, quantitative results for this domain are not interpreted in the main text and are provided only in Supplementary Data S1 and Supplementary File 9 as exploratory extraction states.

Overall, safety occurred in 98 reports, fairness/equity in 61, explainability/interpretability in 155, and economic/resource evaluation in 182. Extraction of privacy/governance/post-deployment information showed very low inter-reviewer reliability, and its numerical findings are thus omitted from main-text interpretation. Not-detected extraction status does not necessarily mean absence from an article (Table 4).

Numerical results for low/moderate reliability concerning clinical outcomes, privacy/monitoring, and technical integration are not included in the main manuscript. Exploratory workflow/technical-integration and implementation-gap extraction results are provided in Supplementary File 9, Exploratory Figures E1 and E2, for audit transparency only; they are not prevalence estimates.

Table 5 summarizes the TA200, FT150 and DX120 validation results with bootstrap 95% confidence intervals. In TA200, original automation achieved 42.5% agreement (95% CI 35.5–49.5), κ = 0.133 (95% CI 0.066–0.204), and Include F1 = 0.428 (95% CI 0.337–0.513); calibrated automation achieved 46.0% agreement (95% CI 39.0–53.0), κ = 0.183 (95% CI 0.100–0.266), and Include F1 = 0.476 (95% CI 0.353–0.583). In FT150, the primary reference comparison yielded 59.3% agreement (95% CI 52.0–67.3), κ = 0.212 (95% CI 0.068–0.356), and Include F1 = 0.558 (95% CI 0.450–0.657); the final adjudicated reference comparison yielded 76.0% agreement (95% CI 68.7–82.7), κ = 0.477 (95% CI 0.346–0.604), and Include F1 = 0.651 (95% CI 0.524–0.758). The latter is post-adjudication concordance, not wholly independent validation. In the same TA200 sample, include sensitivity was 88.9% (40/45) for original automation and 55.6% (25/45) for calibrated automation against the independent reviewer reference. Thus, the increase in F1 was accompanied by lower sensitivity in this comparator-specific sample; these estimates do not measure the sensitivity of the complete human-assisted review workflow (Supplementary File 5).

In the replacement-adjusted DX120 sample, 1411 field comparisons were evaluable. Agreement was 79.4% (cluster-bootstrap 95% CI 77.2–81.7), κ = 0.579 (95% CI 0.534–0.624), AC1 = 0.602 (95% CI 0.557–0.645), precision = 0.843, recall = 0.675, specificity = 0.894, NPV = 0.766, and F1 = 0.750 (95% CI 0.721–0.782). Strict three-level stage agreement was 96.7% (95% CI 93.3–99.2), κ = 0.916 (95% CI 0.818–0.981), and macro-F1 = 0.949 (95% CI 0.889–0.990). Full class-specific metrics and confidence intervals are reported in Supplementary File 9 and the authoritative validation workbook.

In total, the source locked-remediation involved 666 risk flagged files. Prior to the application of New90 integrity overlay, the distribution included 105 Inclusion, 557 Exclusion and four Unclear/F10 files. For re-verification, 90 targeted files were included, 37 of which were still Inclusion and 53 became Exclusion and, therefore, the final distribution was 52 Inclusion, 610 Exclusion and four Unclear/F10. Overall, 3767 reports were considered for eligibility: 1181 were included and 2586 were not included.

The resulting evidence map, which is based on PubMed/MEDLINE data and strongly skewed toward PMC, is made up of 1181 accessible reports on AI-CDSS for clinicians. The taxonomy that was constructed manually and signed off by humans was primarily focused on Clinical validation, while Prospective/user and Implementation/impact evaluation were performed less often. The system could not replicate the clinician-facing threshold with the necessary accuracy and thus replace human moderation, and structured data extraction reliability was dependent on the topic. The main value of this work is establishing translational stages in an auditable evidence map with clear boundaries.

These results agree with previous review studies that highlight the existence of abundant technical evidence but little evidence regarding clinical use [3,4,5,6]. The inclusion of the SWOT analysis from Sallam et al. makes it clear that the identified opportunities in terms of diagnosis and efficiency are threatened by other issues, namely, bias, privacy, transparency, and oversight [9].

This body of work illustrates why real-world data are not synonymous with real clinical use. Retrospective EHR, registry, imaging, laboratory, or waveform data may support clinically relevant validation but do not show that clinicians used the tool or that care changed. The strict eligibility rule therefore required a concrete clinician-facing layer and preserved distinctions among Clinical validation, Prospective/user evaluation, and Implementation/impact evaluation. The final 666-record remediation and 90-record integrity re-verification materially changed the corpus, highlighting the importance of explicit translational criteria and signed human approval.

Extraction of clinical/patient-outcome information showed low inter-reviewer reliability in this review; therefore, these extraction states were not used for corpus-wide quantitative generalization. This is a limitation of the review’s extraction process, not a judgment on the reliability of clinical-outcome research as a field. Future AI-CDSS studies should relate model outputs to clinician actions, process changes, and patient outcomes.

Internal validation was common, while external validation, multicenter validation, and especially temporal validation were rare. Transportability might be affected by factors such as prevalence, measurement, documentation, practice, and structural data differences. External validation does not guarantee long-term stability, and local validation, temporal validation, recalibration, and updating are still necessary [15,16,17,18,19].

Fewer studies included calibration and decision-curve analysis than discrimination. TRIPOD+AI and PROBAST+AI also focus on calibration, generalizability, quality of reporting, and bias in addition to discrimination [23,24]. Since clinical tools usually prompt action above some threshold value, future studies should consider prespecifying threshold values, calibration in the large and slope where relevant, net benefit analysis, and local recalibration or updating.

More general characterizations of entire workflows or layers of use were common. Indicators of technical integration were more problematic, and thus the frequency distribution of these is not discussed in the body of the paper. The impact of workflow depends on task design, interface, timing, training, organizational setting, and accountability systems. Thus, integration must be thought of as a sociotechnical intervention, in terms of who gets the product, when they get it, how they get it, what training comes along with it, how disputes are settled, and what follows.

Explainability or interpretability was detected in 155/1181 (13.1%) reports, while 621/1181 (52.6%) were NR or uncaptured. A missing positive extraction signal does not prove that no explanation was provided; nevertheless, external analyses indicate that clinician-centered evaluation of explanations remains uncommon [8]. Future studies should test whether explanations improve appropriate reliance, error detection, confidence calibration, or decision quality rather than assume that feature importance or saliency is inherently useful.

The extraction results did not provide a reliable corpus-based estimate of prevalence for any of the clinical or patient outcomes. Even if death or disease occurrence is not necessary as the outcome measure in all AI-CDSSs, there needs to be a description of how the output is converted to decisions and processes and ultimately to patient outcomes in each study.

Signals regarding safety and equity/fairness were reported in relatively few papers; nonetheless, the lack of positive extraction of safety signals in the articles considered does not mean their overall lack. The assessment of safety should go beyond average error of models and include false positive and false negative rates, automation bias, alert fatigue, subgroup performance, failure modes of workflows, and possible misuse.

The assessment of fairness should move beyond measures of parity. Subgroup differences may occur due to representation, data quality, measurement, prevalence, access, or care pathways; conversely, equality on one measure does not necessarily mean equal benefit. Fairness should be assessed through representation, subgroup calibration, threshold impact, missingness, access, and change in disparities due to deployment [13,28].

Economic or resource evaluation was detected in 182/1181 reports and showed better field reliability than the exploratory outcome and governance variables. Economic analyses should address acquisition, integration, local validation, training, workflow redesign, maintenance, monitoring, cybersecurity, and the cost of incorrect decisions.

Extraction of privacy/governance/post-deployment information showed very low inter-reviewer reliability. Positive, not-detected, and NR/uncaptured states in this domain should therefore be treated only as exploratory extraction results, not as evidence establishing the presence or absence of governance in the original reports.

It seems clear that there is a link between the gaps identified and current regulatory expectations. In addition to the focus on ethical issues, the WHO highlights the importance of human rights, governance, evaluation and monitoring, describing their guidelines as non-binding [13,14]. FDA issued final guidance on the use of AI for device software functions in PCCP in August 2025 and CDS software in January 2026 with continued support for risk-based monitoring through lifecycle and real-world performance [15,16,17]. The international guidelines set out by the IMDRF N41 and N88 establish principles for the clinical evaluation of SaMD and good machine-learning practices [18,19]. The regulation (EU) 2026/1744 “Digital Omnibus on AI” is currently in effect and has updated the framework and timelines for the implementation of the AI Act [20].

Reporting standards can help align research with these requirements. CONSORT-AI and SPIRIT-AI can be used for the transparent reporting of trials and protocols for AI interventions [21,22]; TRIPOD+AI and PROBAST+AI can be applied to the reporting and critical evaluation of predictive models [23,24]; STARD-AI can be used for diagnostic accuracy reporting [25]; CLAIM provides imaging-specific guidance, including its 2024 revision [26,27]; and FUTURE-AI provides a comprehensive lifecycle framework [28].

Methodological strengths include a comprehensive synthesis of 1181 reports, specification of Clinical validation, Prospective/user evaluation, and Implementation/impact evaluation; a 66-item charting form and a new provenance matrix at the field level; validation of all 3691 PMC identifiers; recording of independent, consensus, and final audit values; prespecified TA200, FT150, and DX120 quality-control modules; remediation of human errors on 666 risk-flagged records; joint signatures on the final eligibility lock and 52 new charted reports; bootstrapped uncertainty that is reproducible; and minimal duplicate-report sensitivity check.

A number of limitations have far-reaching implications. First, the search covered only PubMed/MEDLINE and publications starting from 2020; 2020 was retrospectively noted as a pragmatic design decision. Second, the retrieval summary recorded 1373 of 1449 outside-PMC candidates (94.8%) as not retrieved and all 3691 PMC candidates as assessed. Systematic interlibrary-loan retrieval or author contact was not implemented across all unavailable reports, and no candidate-level retrieved-versus-not-retrieved comparison was available; hence the direction and magnitude of availability bias cannot be quantified. Third, the corpus was not fully independently double-screened and double-extracted. TA200 and FT150 are quality-control modules specific to each comparator; the eligibility criteria and the protocol were revised retrospectively, and there was no risk-of-bias or critical appraisal tool formally used. Fourth, Study_Design was retrospectively mapped back, and 170 reports were not reported/captured. Fifth, the reliability of clinical/patient outcomes, privacy/governance/post-deployment monitoring, and technical integration was low to moderate; numeric results for them are not reported here. Sixth, the unit of analysis is the publication report, and N = 1180 is just a minimal duplicate-report check on the identifier/title level. Documentation limitations affecting five non-included reports are described in Table 1 and Supplementary File 8. TA200 results are comparator-specific and do not establish corpus-wide screening sensitivity.

The assessment of the performance of AI-based CDSS should include calibration, integration into workflow, training of users, safety, and monitoring along with other considerations. Health care organizations need to identify the decision to be supported, the user group, the action threshold, the escalation procedure, and situations under which an output could be overridden.

Validation and implementation by developers are interlinked activities throughout the product lifecycle. Documentation needs to cover data sources, users, error modes, choice of action thresholds, human–AI interaction, implementation context, updating practices, and monitoring plan. Responsibility needs to be defined within health care organizations regarding governance, auditing, adverse event reporting, equity, security, maintenance, and, eventually, retiring of the AI-based system.

Regulatory and policy makers must ensure representativeness of data, human oversight, transparency, post-market surveillance, and controlled model modification. Research must move past accuracy-focused work and examine the impact of AI on clinicians’ practice in terms of when, how, who and at what cost the changes occur.

Future research must concentrate on temporal and external validation, local calibration, prospective silent validation, multicenter implementations, and direct measures of adoption, usability, trust, workload, and clinical outcomes. Prospective safety and equity testing should include subgroup and failure modes testing wherever possible. Economic evaluation needs to start early to gather information about implementation costs and adoption trajectories. Postimplementation research must set out in advance thresholds for action, drift monitoring, need for retraining, governance requirements, and reactions to unanticipated harms. In low-resource settings, local capacity building of data, infrastructure, personnel, and governance needs to occur rather than assuming that a model will transfer without modification [12,28].