This study followed the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 statement [15], the PRISMA extension for diagnostic test accuracy (PRISMA-DTA) [16], the PRISMA extension for network meta-analyses (PRISMA-NMA) [17], the PRISMA extension for Abstracts [18], and the PRISMA literature search extension (PRISMA-S) [19]. Completed reporting checklists are provided in Tables S1 to S4 in Multimedia Appendix 1 [15-19]. The protocol was prospectively registered with PROSPERO (CRD420261362111).

Two investigators (HZ and LL) systematically searched the PubMed, Embase, Web of Science Core Collection, and Cochrane Library databases from inception to May 24, 2026. The search combined controlled vocabulary and free-text terms across 4 concept blocks: ischemic stroke, occlusion location, NCCT, and AI or automated detection. No restrictions on publication date, language, or study type were applied. Citation tracking of included studies and relevant reviews was also performed. The full reproducible search strategy and final database yields are provided in Table S5 in Multimedia Appendix 1. Two reviewers (HZ and LL) independently screened titles, abstracts, and full texts against the eligibility criteria. Disagreements were resolved through discussion, with adjudication by XL when consensus could not be reached.

Eligibility criteria were structured using the participants, index tests, target condition, reference standard, outcomes, and study design framework for diagnostic test accuracy reviews [16]. Participants were adults with suspected AIS who underwent baseline NCCT. Index tests comprised 4 mutually exclusive nodes. Expert readers were senior neuroradiologists, stroke specialists, or experienced radiologists explicitly identified as expert or senior readers or reported as having substantial NCCT interpretation experience in the source publications. Nonexpert readers were nonneuroradiology or non–stroke specialist readers, including general radiologists, emergency physicians, junior radiology or neurology residents, or trainees as specified in the source publications. Unimodal imaging AI comprised fully automated algorithms receiving only NCCT images without clinical information. Clinically informed multimodal AI comprised fully automated algorithms integrating NCCT images with immediately available bedside clinical variables such as the National Institutes of Health Stroke Scale (NIHSS) score and time from symptom onset. Variables requiring laboratory turnaround time, such as blood test results, were excluded. The target condition was predominantly anterior circulation LVO, defined as occlusion of the internal carotid artery or middle cerebral artery M1 segment with or without M2 involvement; anterior circulation cases were required to constitute 90% or more of the study cohort.

The reference standard was CTA in the vast majority of included studies; DSA, the definitive angiographic gold standard, and MRA were accepted as alternative reference standards when available. One included cohort used mixed vascular reference standards and a broader reference standard timing window; its influence was evaluated through prespecified sensitivity analysis. Outcomes required sufficient data for complete 2 × 2 contingency table reconstruction. Study design required within-study head-to-head comparisons involving at least 2 of the 4 prespecified diagnostic nodes to ensure clinically meaningful network connectivity. This head-to-head requirement restricted the primary evidence base to studies capable of informing comparative network inference; otherwise relevant single-node validation studies excluded under this criterion are summarized in Table S6 [20-22] in Multimedia Appendix 1. The study by Olive-Gadea et al [23] was retained because anterior circulation occlusions constituted 95% of the validation cohort, satisfying the predefined anterior circulation threshold; its influence was evaluated in sensitivity analysis.

Eligible AI studies had to evaluate diagnostic performance in validation cohorts independent of model development. Acceptable validation designs included independent external validation, independently assembled validation cohorts, and temporal internal validation. Studies relying solely on training set performance, random hold-out splits, cross-validation, or bootstrapping were excluded from the main analysis. Studies were also excluded if they were limited to posterior circulation occlusions; evaluated CTA-only, computed tomography perfusion–only, or magnetic resonance imaging–based AI; lacked sufficient data for 2 × 2 table reconstruction; were single-arm diagnostic studies; were nonoriginal reports; or used overlapping cohorts. These criteria were intended to preserve clinical comparability and support the plausibility of the transitivity assumption; statistical consistency was evaluated separately.

Two investigators (JM and FY) independently extracted data using a standardized form; XL adjudicated discrepancies. Extracted information included study design, country, center type, reference standard, validation design, cohort size, LVO prevalence, target vessel segments, NCCT acquisition parameters, AI software or model type, reader category, and 2 × 2 diagnostic data. For studies reporting both internal and external validation, external validation data were preferentially extracted. For multi-reader studies, source-reported group-level results were used when available. Otherwise, reader-level results were averaged within the prespecified expertise category and converted to an integer 2 × 2 table; no noninteger cell counts were entered into the binomial model. Study-specific derivation is detailed in Table S7 in Multimedia Appendix 1 [7-9,11,12,23-27]. Rai et al [7] reported 2 nonoverlapping external validation subsets with different node compositions; these subsets were entered separately because merging them would have disrupted the node-level data structure (Tables S8 and S9 in Multimedia Appendix 1 [7-9,11,12,23-27]). Source-reported reader expertise, comparator structure, and classification basis for expert reader and nonexpert reader nodes are summarized in Table S7 in Multimedia Appendix 1 [7-9,11,12,23-27].

Two independent reviewers (BF and BC) assessed risk of bias and applicability using the Prediction Model Risk of Bias Assessment Tool for AI (PROBAST+AI) [28]. Diagnostic accuracy risk of bias and applicability were additionally assessed using the Quality Assessment of Diagnostic Accuracy Studies–3 (QUADAS-3) across the participants, index test, target condition, and analysis domains [29]. Discrepancies were resolved by XL. The Grading of Recommendations Assessment, Development, and Evaluation (GRADE) framework was used to rate certainty for node-specific and major comparative sensitivity and specificity estimates [30]. Risk-of-bias judgments within the GRADE framework were informed by the PROBAST+AI and QUADAS-3 assessments. Domain-level judgments and evidence profiles are provided in Tables S10 to S12 [7-9,11,12,23-29], S13 [30], and S14 [7-9,11,12,23-30] in Multimedia Appendix 1.

Sensitivity quantified correct identification of anterior circulation LVO, and specificity quantified correct exclusion of LVO. Because emergency LVO triage is primarily intended to reduce missed occlusions, sensitivity and false negative consequences were prespecified as the primary clinically relevant dimensions. Specificity and false positive transfer burden were interpreted as secondary clinical dimensions. The diagnostic odds ratio (DOR) and surface under the cumulative ranking curve (SUCRA) were treated as global, exploratory summaries rather than the primary basis for clinical ranking [31].

The Bayesian DTA-NMA was performed in R (version 4.5.2; R Foundation for Statistical Computing) using R2jags. A bivariate hierarchical random-effects model jointly estimated sensitivity and specificity while accounting for potential threshold effects [32,33]. For cohorts contributing more than one diagnostic node, rows were indexed using a shared cohort identifier and modeled using common cohort-level random effects together with cohort-by-node relative random effects, thereby accounting for clustering of diagnostic arms within the same validation cohort. Weakly informative normal priors (mean 0; precision=0.01 [variance=100]) were assigned to logit-transformed sensitivity and specificity parameters. In the primary model, uniform(0, 2) priors were assigned to the between-study SDs, and a uniform(−0.99, 0.99) prior was assigned to the correlation coefficient ρ. Posterior distributions were estimated using Markov chain Monte Carlo (MCMC) simulation with 4 chains, 10,000 burn-in iterations, and 200,000 sampling iterations per chain; chains were thinned every 10 iterations, yielding 80,000 retained posterior draws for inference. Convergence was assessed via trace plot inspection and the potential scale reduction factor, with values below 1.05 considered acceptable [34].

Between-study heterogeneity was quantified using τ on the logit scale [35]. Local inconsistency was assessed through node splitting when an independent indirect comparison was identifiable. Global inconsistency was assessed using the design-by-treatment interaction model, with model fit compared using the deviance information criterion (DIC); ΔDIC was defined as DIC for the inconsistency model minus DIC for the consistency model [36]. SUCRA values were calculated as descriptive summaries of diagnostic hierarchy rather than definitive evidence of clinical superiority [37]. League tables of relative DORs (rDORs) and absolute differences in sensitivity and specificity were generated; the rDOR league table is provided in Table S15 in Multimedia Appendix 1. Clinical utility was evaluated using absolute effects per 1000 patients and Fagan nomograms at pretest probabilities of 20%, 30%, and 49.8% [38]. The 20% scenario was used as the primary clinical illustration for suspected AIS or emergency triage populations, 30% represented confirmed or high-suspicion AIS populations [39,40], and 49.8% represented the enriched median prevalence of the included validation cohorts.

Meta-regression explored 4 covariates: NCCT slice thickness (<3 vs ≥3 mm), M2 occlusion inclusion, validation strategy, and algorithm origin (commercial vs laboratory developed). The validation strategy and algorithm origin covariates were restricted to AI nodes because internal vs external model validation and algorithm development origin do not apply to human visual assessment. Five data structure sensitivity analyses were performed. Sensitivity analysis 1 restricted the network to independent external validation and anterior circulation cohorts and excluded the study by Olive-Gadea et al [23]. Sensitivity analysis 2 excluded the sole laboratory-developed AI model reported by Tolhuisen et al [24]. Sensitivity analysis 3 retained M2-including studies only. Sensitivity analysis 4 removed subset A in the study by Rai et al [7]. Sensitivity analysis 5 excluded the US cohort in the study by Sunwoo et al [25]. These analyses evaluated robustness to anterior circulation restriction, validation design, algorithm origin, M2 inclusion, dual subset handling, and mixed or nonconcurrent reference standard characteristics. Small-study effects were assessed using the Deeks funnel plot asymmetry test [41].

To assess robustness to heterogeneity prior assumptions, an additional prior sensitivity analysis (sensitivity analysis 6) refitted the model after replacing the primary uniform(0, 2) priors for the between-study SDs with weakly informative half-normal(0, 1) priors [42]. The likelihood, node definitions, correlation prior, MCMC settings, convergence criteria, and diagnostic data structure were otherwise unchanged. Sensitivity analysis 6 results were compared with those of the primary model for node-level sensitivity, specificity, and DOR and the exploratory diagnostic hierarchy.

Transitivity was assessed by comparing key potential effect modifiers across studies and nodes, including reader expertise, target vessel definition, M2 inclusion, NCCT section thickness, reference standard, LVO prevalence, validation design, algorithm type, and multimodal clinical inputs (Table S16 in Multimedia Appendix 1).

This study used published aggregate data and did not involve new individual-level patient data. Additional institutional review board approval or informed consent was therefore not required.

Database searches up to May 24, 2026, identified 1775 records (PubMed: n=393, 22.1%; Embase: n=860, 48.5%; Web of Science: n=486, 27.4%; Cochrane Library: n=36, 2%). After deduplication and screening, 10 independent studies [7-9,11,12,23-27] encompassing 11 validation cohorts, 28 study node arms, and 3632 patients met the eligibility criteria (Figure 2A). Reasons for exclusion of the single-arm studies are detailed in Table S6 [20-22] in Multimedia Appendix 1.

The 10 included studies were published between 2020 and 2026 and were conducted in South Korea, the United States, Spain, the United Kingdom, Germany, Greece, Chile, Brazil, and the Netherlands. Baseline characteristics are summarized in Table 1, with additional validation cohort demographics and NCCT acquisition details provided in Tables S8 and S9 in Multimedia Appendix 1 [7-9,11,12,23-27]. All included studies were retrospective validation studies. In total, 90% (9/10) of the studies evaluated AI software developed by commercial companies, whereas 10% (1/10) of the studies evaluated a laboratory-developed AI model. A total of 90% (9/10) of the studies used independent external validation, and 10% (1/10) used temporal internal validation. CTA was the reference standard in 90% (9/10) of the studies, comprising 3392 participants; 10% (1/10) of the studies, comprising 240 participants, used mixed CTA, MRA, and DSA reference standards. Potential effect modifiers varied across studies, particularly in reader expertise, M2 inclusion, NCCT section thickness, LVO prevalence, and multimodal clinical inputs (Table S16 in Multimedia Appendix 1).

Complete 2 × 2 diagnostic data for all 28 study node arms are shown in Table 2. Expert readers were predominantly senior neuroradiologists, stroke specialists, or experienced radiologists, whereas nonexpert readers included general radiologists, emergency physicians, and junior radiology or neurology trainees, as reported in the source studies. These data formed the basis of the Bayesian DTA-NMA and enabled comparison across the 4 predefined diagnostic paradigms (Figure 2B). Node distribution was k=7 for expert readers, k=7 for nonexpert readers, k=11 for unimodal imaging AI, and k=3 for clinically informed multimodal AI. Individual study-level forest plots for sensitivity, specificity, and DOR are provided in Figures S1 to S4 in Multimedia Appendix 1.

The evidence network was connected across the 4 diagnostic paradigms, with edge thickness proportional to the volume of within-study head-to-head comparisons (Figure 3). The clinically informed multimodal AI node was connected to human-reader nodes only through the unimodal imaging AI node; comparisons with human readers were therefore entirely indirect. MCMC diagnostics showed satisfactory convergence for node-level sensitivity, specificity, and DOR estimates, with adequate trace plot mixing, stable posterior density overlays, and potential scale reduction factor values below 1.05. The design-by-treatment interaction model yielded a ΔDIC of −0.19, representing negligible separation in model fit between the inconsistency and consistency models. No compelling global inconsistency signal was identified, although node splitting suggested potential local inconsistency for sensitivity between expert and nonexpert readers and the sparse network limited the power to detect inconsistency. Detailed direct and indirect evidence structures and posterior inconsistency factors are provided in Table S17 in Multimedia Appendix 1. Convergence and consistency diagnostics are shown in Figures S5 to S8 in Multimedia Appendix 1.

Validation-stage PROBAST+AI assessments were low risk in 90% (9/10) of the studies and unclear in 10% (1/10), whereas complementary QUADAS-3 assessments identified high risk in the participants domain in all studies (10/10, 100%) and high participant applicability concerns in 90% (9/10) of the studies. Additional study-specific concerns were identified in the index test, target condition, and analysis domains; overall QUADAS-3 risk of bias and overall applicability concerns were high in all studies (10/10, 100%; Figure 4; Tables S10-S12 [7-9,11,12,23-29] and Figure S9 [29] in Multimedia Appendix 1). GRADE certainty was low for 7 of 8 node-specific estimates and moderate for unimodal imaging AI specificity. Comparative certainty was low for unimodal imaging AI vs either reader node and for clinically informed multimodal AI vs unimodal imaging AI and very low for clinically informed multimodal AI vs either reader node (Tables S13 [30] and S14 [7-9,11,12,23-30] in Multimedia Appendix 1).

Under the prespecified clinical interpretation framework, sensitivity and false negative burden were treated as the primary dimensions for emergency LVO triage, whereas specificity and false positive transfer burden were treated as secondary dimensions. Pooled sensitivity and specificity estimates are summarized in Figure 5 and Figure 6 and in Figures S10 and S11 in Multimedia Appendix 1. Clinically informed multimodal AI had a sensitivity of 0.81 with a 95% credible interval of 0.64 to 0.92 and specificity of 0.92 (95% credible interval 0.80-0.98). Unimodal imaging AI had a sensitivity of 0.78 (95% credible interval 0.68-0.86) and specificity of 0.88 (95% credible interval 0.81-0.94). Expert readers had a sensitivity of 0.62 (95% credible interval 0.48-0.75) and specificity of 0.86 (95% credible interval 0.77-0.93). Nonexpert readers had a sensitivity of 0.60 (95% credible interval 0.45-0.75) and specificity of 0.86 (95% credible interval 0.75-0.93). These estimates indicated a clearer signal for sensitivity than for specificity.

Exploratory DOR estimates followed the same broad pattern: clinically informed multimodal AI had a DOR of 75.42 (95% credible interval 15.63-235.86), unimodal imaging AI had a DOR of 30.89 (95% credible interval 14.19-60.27), expert readers had a DOR of 11.53 (95% credible interval 5.15-22.48), and nonexpert readers had a DOR of 10.94 (95% credible interval 4.09-24.08; Figure 5; Figure S12 in Multimedia Appendix 1).

The rDOR league table showed higher DOR point estimates for AI diagnostic nodes than for human reader nodes, but these comparisons were interpreted as exploratory summaries rather than direct clinical rankings (Table S15 in Multimedia Appendix 1). The clearest relative sensitivity signal was observed for unimodal imaging AI, which showed higher sensitivity than expert readers and nonexpert readers by 0.16 (95% credible interval 0.03-0.29) and 0.18 (95% credible interval 0.03-0.32), respectively (Figure 7). Clinically informed multimodal AI had higher sensitivity point estimates than human reader nodes, but the corresponding credible intervals were wide and crossed or touched 0. Its rDOR comparison with unimodal imaging AI was also inconclusive at 2.04 (95% credible interval 0.55-7.83). All specificity differences had 95% credible intervals crossing 0 (Figure 7).

SUCRA rankings were interpreted as descriptive summaries of diagnostic hierarchy rather than definitive evidence of clinical superiority. Clinically informed multimodal AI had the highest SUCRA values for sensitivity (87.8%), specificity (83.3%), and DOR (94.8%), followed by unimodal imaging AI for sensitivity (76.3%) and DOR (70.2%). Because clinically informed multimodal AI was supported by only 30% (3/10) of the studies and relied entirely on indirect evidence for comparisons with human readers, its highest point estimates should be treated as exploratory rather than as proof of clinical superiority.

Between-study heterogeneity (τ) on the logit scale was 0.49 (95% credible interval 0.10-0.91) for sensitivity, 0.61 (95% credible interval 0.12-1.06) for specificity, and 0.51 (95% credible interval 0.17-0.95) for log-DOR, with relatively wide credible intervals indicating limited precision. The sensitivity-specificity correlation was also imprecisely estimated (ρ=−0.58, 95% credible interval −0.97 to 0.34), precluding a firm conclusion regarding a clinically meaningful threshold-related effect. All 4 meta-regression covariates (NCCT slice thickness, M2 segment inclusion, validation strategy, and algorithm origin) had 95% credible intervals crossing 0 (Table S18 in Multimedia Appendix 1). Given the limited statistical power of 10 studies and the single laboratory-developed AI row for the commercial vs laboratory-developed AI comparison, these analyses should be considered exploratory and should not be interpreted as evidence that these factors have no influence on diagnostic performance.

Across 6 sensitivity analyses (Table S19 in Multimedia Appendix 1), the exploratory DOR hierarchy remained broadly stable. Sensitivity analyses 1 to 5 addressed validation design, anterior circulation restriction, algorithm origin, M2 inclusion, dual subset handling, and mixed or nonconcurrent reference standard characteristics. Sensitivity analysis 6, which replaced the primary uniform(0, 2) between-study SD priors with half-normal(0, 1) priors, produced no material change in node-level sensitivity, specificity, or DOR estimates or the exploratory diagnostic hierarchy. AI diagnostic nodes remained directionally favored over human reader nodes for sensitivity and DOR, whereas specificity differences remained unclear.

Clinical utility was primarily illustrated at a 20% pretest probability, approximating suspected AIS or emergency triage populations. Per 1000 patients, unimodal imaging AI yielded approximately 156 true positives, 44 false negatives, 92 false positives, and 708 true negatives compared with 125, 75, 112, and 688 for expert readers, respectively, and 121, 79, 113, and 687 for nonexpert readers, respectively. Corresponding absolute outcomes at 30% and 49.8% pretest probabilities are provided in Table S20 in Multimedia Appendix 1, with Fagan nomograms for all 3 scenarios shown in Figures S13 to S15 in Multimedia Appendix 1. The 49.8% scenario represents the enriched median prevalence of the included validation cohorts rather than routine emergency triage prevalence. The Deeks test was uninformative because of the small number of studies (P=.76; Figure S16 [41] in Multimedia Appendix 1).

In this systematic review and Bayesian DTA-NMA of 10 studies and 3632 patients, NCCT-based AI showed a comparative sensitivity signal for emergency anterior circulation LVO triage. Sensitivity and false negative reduction rather than specificity were the clearest dimensions of potential clinical value. For context, these pooled sensitivities compare favorably with the sensitivity of approximately 52% for the hyperdense artery sign [10], suggesting that AI-assisted NCCT assessment may improve LVO recognition beyond reliance on this conventional visual marker alone. The relative evidence was strongest for NCCT-only AI, whereas the higher point estimates for clinically informed multimodal AI remained exploratory because that node was sparse and relied entirely on indirect evidence for comparisons with human readers. This review extends prior syntheses of NCCT-based AI for LVO and commercial platforms by isolating the NCCT-before-CTA decision point and embedding human reader comparators within the same evidence network [13,14]. Overall, the evidence supports potential triage assistance, but diagnostic certainty should not be conflated with implementation certainty. The GRADE ratings in this review apply to diagnostic accuracy estimates in validation cohorts, not to workflow effectiveness, transfer appropriateness, EVT delivery, or patient outcomes.

CTA remains the first-line noninvasive confirmatory test for anterior circulation LVO, and DSA remains the definitive invasive angiographic reference standard. NCCT-based AI should therefore not be framed as a replacement for CTA, a rule-out test, or an autonomous transfer decision system. Its clinically plausible role is earlier in the pathway: a human-in-the-loop signal that may prompt urgent image review, CTA prioritization, tele-stroke consultation, stroke team notification, or transfer discussion when vascular imaging is delayed or operationally constrained. Any reduction in missed LVOs must be balanced against false positive escalation, which may increase unnecessary CTA and contrast exposure, avoidable clinical activations or transfer discussions, workload, alert fatigue, and workflow disruption. AI-positive signals should therefore accelerate appropriate vascular confirmation rather than substitute for it.

The network nodes should be interpreted as workflow functions rather than product rankings. Expert readers provide a specialist benchmark, whereas nonexpert readers approximate first-contact or off-hours interpretation. These are the settings in which escalation is most likely to be delayed. Such settings may also be particularly susceptible to automation bias if AI output is given disproportionate weight during subsequent image interpretation or clinical decision-making, potentially reducing independent critical assessment of the NCCT. This concern may be especially relevant for junior or nonspecialist readers, who had the lowest pooled sensitivity in our network. However, the included retrospective validation studies did not evaluate clinician reliance on AI output, override behavior, or changes in unaided interpretation after AI exposure; therefore, the magnitude of automation bias cannot be quantified from the current evidence. NCCT-based AI should consequently remain an adjunctive human-in-the-loop prompt rather than a substitute for independent clinical assessment and confirmatory vascular imaging. From an operational perspective, unimodal imaging AI can run immediately after image acquisition and does not depend on bedside data entry. The higher point estimates observed for clinically informed multimodal AI may partly reflect the incorporation of additional clinical information, including the NIHSS in all 3 included models and symptom onset time in 1. However, the current network cannot isolate the incremental contribution of these variables from other between-study differences, and this apparent advantage remains uncertain and hypothesis generating because the node was supported by only 3 studies and relied entirely on indirect evidence for comparisons with human readers. The relevant clinical question is therefore not whether AI outperforms ideal specialist interpretation under controlled conditions but whether an early signal can accelerate vascular imaging, specialist review, or transfer discussion in time-sensitive workflows.

The restrictive eligibility criteria made the network smaller but more interpretable. By requiring validation independent of model development, NCCT input, anterior circulation LVO, within-study head-to-head comparisons, and reconstructible 2 × 2 data, the review prioritized methodological comparability and interpretability over breadth. Accordingly, the included evidence represents comparative NCCT-based validation studies rather than the complete validation literature for NCCT-based LVO detection. The resulting evidence can frame a plausible escalation role, but it cannot estimate product-specific performance, workflow effectiveness, or patient benefit with precision. Generalizability and indirect comparison validity remain constrained by retrospective enriched validation cohorts and by residual variation in transitivity-related modifiers, including reader expertise, target vessel composition, NCCT acquisition parameters, reference standard characteristics, validation design, and AI input variables. Statistical network connectivity does not necessarily establish clinical exchangeability; accordingly, indirect comparisons should be interpreted as directional comparative signals rather than definitive evidence that AI intrinsically outperforms human readers. The sparse network also limited the power to detect inconsistency, particularly for comparisons involving the multimodal AI node. Shared cohort-level effects were modeled for studies evaluating AI and human readers in the same patients, but aggregate 2 × 2 data precluded explicit modeling of within-patient AI-reader correlation. In addition, category-level averaging of multiple readers may have attenuated interreader variability, and the available data did not support a consistent reader-level sensitivity analysis. The robustness of the diagnostic hierarchy to an alternative half-normal heterogeneity prior supports statistical stability of the Bayesian synthesis, but it does not overcome the need for prospective workflow validation. Together, these constraints define where prospective evaluation must occur: lower-prevalence emergency populations; CTA-constrained or off-hours pathways; sites with different scanner protocols; and predefined action pathways linking an AI-positive NCCT alert to vascular imaging, tele-stroke consultation, or transfer discussion.

Future studies should move from stand-alone diagnostic accuracy to pathway effects. Deployment evaluations should predefine how an AI-positive NCCT alert is acted on and measure picture archiving and communication system integration, alert latency, clinician response, override behavior, false positive transfer burden, alert fatigue, NIHSS data entry burden, site-level generalizability, and equity of access [43]. Clinical deployment also requires appropriate IT infrastructure; integration with existing imaging and stroke workflows; continued clinician oversight; and, for multimodal systems, structured electronic health record interfaces or other standardized real-time access to relevant clinical variables. Early real-world studies have begun to evaluate NCCT-based AI implementation, whereas a cluster randomized clinical trial of a related CTA-based LVO workflow suggested that AI-assisted notification may shorten treatment times. However, prospective evidence demonstrating improved patient outcomes specifically from NCCT-based AI remains limited [44,45]. Prospective multicenter studies should also prespecify subgroup analyses by age, sex, stroke severity, scanner manufacturer, imaging protocol, hospital type, geographic setting, and relevant demographic groups to assess whether diagnostic performance and clinical utility are consistent across patient populations and implementation environments. Stroke-specific end points should include door-to-CTA time, door-in-door-out time, door-to-puncture time, transfer appropriateness, and 90-day modified Rankin Scale outcomes. Without predefined action pathways, improved diagnostic sensitivity may not translate into faster reperfusion or better functional outcomes. Future reports should also follow current AI-specific prediction model and diagnostic accuracy reporting guidelines [46,47].

Taken together, the current evidence supports prospective evaluation of NCCT-based AI as a bounded escalation and prioritization signal before or alongside confirmatory vascular imaging, with the clearest comparative signal observed for unimodal imaging AI sensitivity. The current evidence does not support CTA replacement, LVO rule-out, autonomous transfer decisions, or EVT decisions. Prospective workflow-integrated validation is required before accuracy evidence can justify deployment claims, reimbursement decisions, or protocolized changes in stroke triage pathways.