Artificial intelligence for detecting autism spectrum disorder: a systematic review and meta-analysis.
Frontiers in public health · 2026
Abstract originale
BACKGROUND: Autism spectrum disorder (ASD) is a heterogeneous neurodevelopmental condition, and early identification is essential for timely intervention. Conventional diagnosis relies on clinical interviews, behavioral observations, caregiver reports, and standardized tools, which are time-consuming and resource-dependent. Artificial intelligence (AI) offers opportunities for screening and adjunctive diagnosis, but studies vary in data sources, model types, and validation methods, requiring systematic evaluation. METHODS: We searched PubMed, Embase, the Cochrane Library, Web of Science, and IEEE Xplore for studies of AI-based ASD detection. Eligible studies were required to provide ASD-versus-non-ASD diagnostic-accuracy data that could be extracted or reliably reconstructed at the independent participant or case level. Risk of bias and applicability were assessed using a modified QUADAS-AI tool. Pooled sensitivity and specificity were estimated with a bivariate Reitsma random-effects model. HSROC AUCs were calculated with bias-corrected and accelerated (BCa) 95% confidence intervals based on 5,000 study-level bootstrap replicates and were omitted when SROC fits were unstable. Sensitivity analyses addressed dataset overlap, model selection, and reference-standard quality. RESULTS: Of 17,387 records, 26 studies were included. Pooled sensitivity was 0.908 (95% CI: 0.861-0.940), pooled specificity was 0.868 (95% CI: 0.830-0.898), and the HSROC AUC was 0.936 (BCa 95% CI: 0.860-0.973). A dataset-independent analysis of 21 studies yielded lower estimates (sensitivity 0.870, specificity 0.841, AUC 0.900). Leave-one-out results were generally stable. Funnel-plot asymmetry was not significant in the primary analysis and varied in direction and statistical significance across sensitivity analyses. CONCLUSIONS: AI-based models showed relatively high pooled diagnostic performance for ASD detection, but substantial heterogeneity, methodological and applicability concerns, limited external validation, and potential non-independence of underlying datasets limit the certainty and generalizability of the evidence. Funnel-plot analyses did not provide consistent evidence of conventional small-study effects or selective reporting. AI should therefore be considered an adjunct rather than a standalone diagnostic tool. Prospective multicenter validation in representative populations, participant-level evaluation, clearly defined reference diagnoses, prespecified models and operating thresholds, and independent evaluation datasets are needed before broader clinical implementation.
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Artificial intelligence for detecting autism spectrum disorder: a systematic review and meta-analysis
Background
Autism spectrum disorder (ASD) is a heterogeneous neurodevelopmental condition, and early identification is essential for timely intervention. Conventional diagnosis relies on clinical interviews, behavioral observations, caregiver reports, and standardized tools, which are time-consuming and resource-dependent. Artificial intelligence (AI) offers opportunities for screening and adjunctive diagnosis, but studies vary in data sources, model types, and validation methods, requiring systematic evaluation.
Methods
We searched PubMed, Embase, the Cochrane Library, Web of Science, and IEEE Xplore for studies of AI-based ASD detection. Eligible studies were required to provide ASD-versus-non-ASD diagnostic-accuracy data that could be extracted or reliably reconstructed at the independent participant or case level. Risk of bias and applicability were assessed using a modified QUADAS-AI tool. Pooled sensitivity and specificity were estimated with a bivariate Reitsma random-effects model. HSROC AUCs were calculated with bias-corrected and accelerated (BCa) 95% confidence intervals based on 5,000 study-level bootstrap replicates and were omitted when SROC fits were unstable. Sensitivity analyses addressed dataset overlap, model selection, and reference-standard quality.
Results
Of 17,387 records, 26 studies were included. Pooled sensitivity was 0.908 (95% CI: 0.861–0.940), pooled specificity was 0.868 (95% CI: 0.830–0.898), and the HSROC AUC was 0.936 (BCa 95% CI: 0.860–0.973). A dataset-independent analysis of 21 studies yielded lower estimates (sensitivity 0.870, specificity 0.841, AUC 0.900). Leave-one-out results were generally stable. Funnel-plot asymmetry was not significant in the primary analysis and varied in direction and statistical significance across sensitivity analyses.
Conclusions
AI-based models showed relatively high pooled diagnostic performance for ASD detection, but substantial heterogeneity, methodological and applicability concerns, limited external validation, and potential non-independence of underlying datasets limit the certainty and generalizability of the evidence. Funnel-plot analyses did not provide consistent evidence of conventional small-study effects or selective reporting. AI should therefore be considered an adjunct rather than a standalone diagnostic tool. Prospective multicenter validation in representative populations, participant-level evaluation, clearly defined reference diagnoses, prespecified models and operating thresholds, and independent evaluation datasets are needed before broader clinical implementation.
1Introduction
Autism spectrum disorder (ASD) is a neurodevelopmental condition characterized by persistent deficits in social communication and social interaction, together with restricted interests and repetitive or stereotyped patterns of behavior (1). ASD is clinically heterogeneous, with substantial inter-individual variation in symptom severity, language and cognitive abilities, sensory and motor features, co-occurring conditions, and functional impairment. This heterogeneity complicates early identification and accurate diagnosis (2).
The reported prevalence of ASD has increased over recent decades. Globally, epidemiological evidence suggests that approximately 1 in 100 children is affected by ASD (3). In Asia, particularly Southeast Asia, prevalence estimates are lower, at approximately 6 per 1,000 individuals (4). In contrast, 2022 surveillance data from the US Autism and Developmental Disabilities Monitoring (ADDM) Network reported a prevalence of 32.2 per 1,000 among 8-year-old children across 16 monitoring sites, equivalent to approximately 1 in 31 children identified with ASD (5). Nevertheless, prevalence estimates differ across studies, owing to variations in study period, age range, diagnostic criteria, screening approaches, and surveillance systems. These trends, together with the growing demand for ASD-related services, highlight the need for efficient, objective, and scalable strategies to support ASD screening and diagnosis.
Early identification of ASD is essential for enabling timely intervention and improving developmental outcomes. Detecting ASD-related risks in early childhood and initiating prompt intervention may alleviate core symptoms and enhance social communication, adaptive functioning, and long-term development (6–8). However, ASD cannot be confirmed by a single laboratory test, biomarker, or neuroimaging examination. Its diagnosis relies primarily on multidisciplinary clinical assessment, including clinical interviews, behavioral observations, caregiver reports, and standardized diagnostic instruments. Although these approaches remain the diagnostic standard, they are time-intensive, resource-demanding, and dependent on highly trained professionals, which limits their accessibility in primary care, educational, and resource-constrained settings (9, 10). Early recognition and differential diagnosis are further complicated by developmental changes in ASD symptoms and frequent co-occurrence with conditions such as attention-deficit/hyperactivity disorder, language delay, intellectual disability, and anxiety disorders (9). These challenges underscore the need for efficient, objective, and scalable tools to support ASD screening and diagnostic prediction.
Artificial intelligence (AI) has increasingly been applied to ASD screening, diagnostic support, and risk prediction. Machine learning and deep learning models are capable of extracting latent representations from high-dimensional and multimodal data, enabling the identification of ASD-related patterns. Prior studies have reported promising predictive performance using approaches such as support vector machines (SVM), k-nearest neighbors (KNN), and deep learning (DL) for ASD classification and diagnosis (11–15). For instance, Kong et al. combined brain connectivity features with a deep neural network classifier for ASD classification (16), while Guo et al. (17) proposed a deep neural network-based feature selection method for childhood ASD diagnosis that outperformed conventional methods such as elastic net. In addition, EEG preprocessing, including artifact removal, is an important component of EEG-based ASD identification because preprocessing quality may affect subsequent feature extraction and classification (18). Collectively, these findings indicate that AI models can capture ASD-relevant patterns across diverse data sources and provide auxiliary support for ASD screening and diagnosis. Nevertheless, many existing models are constrained by task-specific designs, single-modality data, and relatively small sample sizes, and their generalizability and real-world applicability remain insufficiently validated.
AI-based studies on ASD screening and diagnostic prediction have incorporated a wide range of data modalities, including eye tracking, EEG, functional near-infrared spectroscopy (fNIRS), video, audio, motor behaviors, electronic health records, clinical text, and other biological or developmental measures (19–24). These modalities provide complementary information on the complex and heterogeneous ASD phenotype. In this context, multimodal AI approaches may be particularly valuable, as they integrate behavioral, neurophysiological, clinical, and developmental data to better characterize diverse ASD presentations. Beyond improving objectivity and scalability, AI-based prediction may facilitate the detection of subtle patterns that are difficult to capture through conventional assessments. Nevertheless, clinical utility depends not only on predictive accuracy but also on implementability, cost, accessibility, and feasibility in real-world settings. Although MRI and genetic testing can provide important neurobiological insights, their reliance on specialized equipment, standardized protocols, and trained personnel limits their applicability in primary screening, educational settings, and large-scale implementation.
Despite rapid advances in AI-based ASD screening and diagnostic prediction, the current evidence remains highly heterogeneous with respect to data modalities, model architectures, sample characteristics, validation strategies, and outcome reporting. In addition, some reported estimates of high diagnostic accuracy may be overoptimistic because of small sample sizes, exclusive reliance on internal validation, lack of clinical control groups, potential data leakage, and inconsistencies in the unit of analysis. A systematic review and meta-analysis is therefore warranted to synthesize existing evidence and quantitatively evaluate the diagnostic performance of relatively low-burden AI-assisted tools for ASD screening and diagnostic support. Accordingly, this study aims to systematically review and meta-analyze the diagnostic performance of such tools, while further assessing their applicability and scalability across data sources, model types, validation strategies, and potential clinical scenarios. These findings may inform the development and translation of AI-assisted approaches for early ASD screening, risk stratification, and clinical decision-making.
Accordingly, this review aims to provide a clinically oriented synthesis of AI-assisted ASD detection, with a focus on relatively low-burden and scalable approaches across behavioral, clinical, neurophysiological, eye-tracking/video-audio, retinal or facial imaging, and multimodal data. Beyond summarizing diagnostic performance, we critically evaluate the consistency, robustness, and generalizability of the available evidence across key study characteristics. By considering diagnostic performance alongside evidence quality and clinical applicability, this review seeks to clarify the current potential, limitations, and translational relevance of AI-assisted approaches for ASD screening and diagnostic support.
2Methods
This systematic review and meta-analysis was designed and reported in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses of Diagnostic Test Accuracy Studies (PRISMA-DTA) guidelines. The completed PRISMA-DTA checklist is provided in Supplementary Table S1. The review was registered with PROSPERO (CRD420251270564).
2.1Inclusion criteria
Studies were included if they met the following criteria: (1) original research involving human participants; (2) development or validation of predictive models based on artificial intelligence, machine learning, or deep learning for the diagnosis, detection, or screening of ASD; (3) application of the model to ASD prediction or classification in comparison with a non-ASD group; (4) use of clinical, behavioral, EEG/fNIRS, eye-tracking, video, audio, imaging data, including retinal or facial imaging, or multimodal data; (5) inclusion of both ASD and non-ASD participants, with sufficient diagnostic accuracy data to extract or reconstruct a 2 × 2 contingency table; and (6) application of cross-validation, hold-out validation, internal validation, or external validation with reported diagnostic performance.
2.2Exclusion criteria
Studies were excluded if they met any of the following criteria: (1) non-human studies, non-original research, or non-peer-reviewed publications; (2) non-English publications; (3) studies that did not develop or validate predictive models based on artificial intelligence, machine learning, or deep learning for ASD diagnosis, detection, or screening; (4) prediction or classification tasks that did not permit evaluation of ASD versus a non-ASD group for diagnostic-accuracy assessment, including population-surveillance case-ascertainment tasks that did not correspond to the clinically oriented ASD screening, detection, or diagnostic-prediction task of this review; (5) absence of non-ASD controls or insufficient diagnostic accuracy data to extract or reconstruct a 2 × 2 contingency table at the independent participant or case level; (6) studies reporting only training-set performance without cross-validation, hold-out validation, internal validation, or external validation; and (7) studies primarily based on structural or functional brain magnetic resonance imaging (MRI/fMRI), as the review was operationally focused on relatively low-burden and scalable approaches for ASD screening and diagnostic support.
The exclusion of studies primarily based on structural or functional brain MRI/fMRI was an operational restriction applied during review conduct and was not explicitly prespecified in the PROSPERO registration, which broadly listed neuroimaging among potentially eligible modalities.
2.3Data sources and search strategy
We systematically searched PubMed, Embase, Web of Science, the Cochrane Library, and IEEE Xplore from inception to September 30, 2025, to identify original studies that applied artificial intelligence, machine learning, or deep learning methods for ASD diagnosis, detection, or screening, prediction, or classification. The search strategy combined controlled vocabulary terms, including MeSH and/or Emtree terms, with free-text keywords. No restrictions were applied on publication year or geographic region. Detailed search strategies for PubMed, Embase, Web of Science, the Cochrane Library, and IEEE Xplore are provided in Supplementary Table S2.
2.4Study selection
Study selection was carried out in two stages based on the operational inclusion and exclusion criteria defined for this review. All records retrieved from the searches were first imported into EndNote. Duplicate records identified during reference management were removed before title and abstract screening. Two reviewers (QW and QHW) then independently screened the titles and abstracts of the remaining records to identify potentially eligible studies. The same reviewers independently assessed the full texts of potentially eligible articles to determine final eligibility. Any disagreements were resolved through discussion, and, when necessary, a third reviewer (RL) was consulted. For the final quantitative synthesis, all potentially eligible studies were additionally verified with particular attention to the unit of analysis and the availability of diagnostic-accuracy data at the participant or case level. Studies were excluded if the reported 2 × 2 data were based on repeated lower-level observations, such as images, signal segments, or sessions, rather than independent participants or cases. Studies were also excluded when the reported validation results did not allow a reliable participant- or case-level 2 × 2 contingency table to be extracted or reconstructed. Eligibility was further reassessed to ensure that the prediction task was consistent with the clinically oriented ASD screening, detection, or diagnostic-prediction scope of the review.
2.5Data extraction, threshold handling, and model categorization
Data extraction was independently performed by two investigators (QW and QHW) using a predesigned standardized form. The following information was collected: first author, publication year, country where the study was conducted, study design, participant characteristics, participant-level cohort/sample size, unit of analysis, type of AI model, input variables, validation method, dataset source and potential dataset overlap, and model performance metrics, including sensitivity, specificity, accuracy, and the area under the receiver operating characteristic curve (AUC). Disagreements were resolved through discussion, and a third investigator (RL) was consulted when consensus could not be reached.
To facilitate structured comparisons across the included studies, the extracted characteristics were categorized by age group, data modality, algorithm family, and validation strategy. Age groups were classified as pediatric, adult/mixed-age, or unclear age. Data modality was defined according to the primary source of information used for ASD detection and categorized as clinical/behavioral, EEG/fNIRS, eye-tracking/video-audio, multimodal, or imaging. Among the 26 included studies, the EEG/fNIRS category was represented exclusively by EEG studies and is therefore reported as EEG in the subgroup analyses. Algorithms were classified according to their principal model family as support vector machine (SVM), ensemble methods other than random forest, decision tree, convolutional neural network (CNN), k-nearest neighbors (KNN), logistic regression, random forest, RNN/LSTM, or other/unclear. Validation strategy was classified according to the validation approach associated with the diagnostic-accuracy estimate retained for analysis as cross-validation, hold-out validation, external validation, or other/unclear. External validation referred to evaluation of the retained model in a dataset or population independent of the data used for model development and tuning. These categories informed the quantitative subgroup analyses and comparative narrative synthesis.
For classification models, we did not apply a uniform classification threshold across studies. Instead, we used the performance estimates reported in the original studies at their main operating thresholds. When multiple candidate thresholds were reported, we used the operating point designated by the original authors as primary, final, or recommended; otherwise, the operating point corresponding to the main validation or test result was used. If the threshold was not explicitly stated but sufficient data were provided to reconstruct a 2 × 2 contingency table, such as sensitivity, specificity, and the numbers of ASD and non-ASD participants, the reported estimates were regarded as reflecting the main operating point of the original study. Studies that reported only AUC, accuracy, or other overall performance measures, without enough information to extract or reconstruct a participant- or case-level 2 × 2 table, were excluded. For each included study, a 2 × 2 contingency table containing true positives, false negatives, false positives, and true negatives was extracted directly or reconstructed from the available data. When performance was reported only as an average across repeated cross-validation or repeated hold-out analyses, these summary estimates were not converted back into participant-level integer counts unless a reliable participant- or case-level 2 × 2 table could be established from the reported results. Only 2 × 2 tables representing participant- or case-level diagnostic classifications were used. When multiple images, signal segments, trials, or other repeated observations were available for the same participant, lower-level observations were not treated as independent diagnostic units; the diagnostic result had to be reported or reconstructable at the participant level. For studies reporting multiclass outputs, data were used only when the reported results permitted an unambiguous reconstruction of the binary ASD-versus-non-ASD classification at the participant level.
When a study reported more than one eligible AI model, we preferentially used the results from the model prespecified or explicitly designated by the original authors as the primary or final model. If no primary or final model was specified, we selected the best-performing eligible model or configuration from the validation or test phase based on the principal performance measure reported in the original study. For the model-selection sensitivity analysis, studies were classified into three mutually exclusive groups: (1) prespecified/author-designated primary or final model, in which the study-level estimate was derived from a model prespecified or explicitly identified by the original authors as primary or final; (2) reviewer-selected best-performing model, in which the review team selected the best-performing result from multiple eligible models or configurations because no primary or final model had been specified; and (3) single eligible model, in which only one model met the eligibility criteria and no model-selection decision was required.
This study-level selection framework was used to avoid within-study double-counting of participants across multiple model estimates or operating thresholds and to improve reproducibility when studies reported multiple models or thresholds. Potential non-independence across different reports was assessed separately using the reported dataset source or underlying cohort information. Reports drawing on the same named repository or on clearly or probably overlapping participant cohorts were flagged as potentially non-independent and documented in Table 1. Cross-study dataset overlap was addressed separately in the dataset-independent sensitivity analysis described in Section 2.7. The potential influence of review-level model selection on the pooled estimates was also examined in sensitivity analysis.
Table 1Characteristics of the 26 included studies and participant-level analytic data.
No. References Country/region Participant–level 2 × 2 analytic sample (ASD/total) Participant–level cohort/sample size Unit of analysis Age group Task Data modality Algorithm family Validation strategy Model–selection strategy Reference standard Dataset source Overlap flag
1 Wall et al. (29) USA 612/627 627 participants in primary classification (612 ASD, 15 non–spectrum); additional ASD–only validation cohorts reported Participant/ADOS Module 1 record Adult/Mixed Diagnosis/detection Clinical/Behavioral Decision Tree Cross–validation Author–designated primary/final Clearly defined AGRE (development/primary); Boston Autism Consortium and SSC (additional validation) Potential overlap: ADOS repositories
2 Duda et al. (26) USA 789/807 807 participants in selected analysis (789 ASD, 18 non–ASD); 2,616 ADOS Module 1 records reported overall Participant/ADOS Module 1 record Pediatric Diagnosis/detection Clinical/Behavioral Decision Tree External validation Single eligible model Unclear/insufficient AC/SSC/SVIP/AGRE/NDAR Potential overlap: ADOS repositories
3 Kosmicki et al. (30) USA 1,924/2,138 4,540 individuals across ADOS Modules 2/3; evaluation subset n=2,138 Participant/ADOS record Pediatric Diagnosis/detection Clinical/Behavioral Support Vector Machine External validation Reviewer–selected best–performing Clearly defined AC/SSC/AGRE/NDAR/SVIP Potential overlap: ADOS repositories
4 Tariq et al. (31) USA 33/66 66 children in prospective validation (33 ASD, 33 non–ASD); development cohort excluded from meta–analysis Participant/validation video (1 per child) Pediatric Diagnosis/detection Eye–tracking/video–audio Logistic Regression External validation Author–designated primary/final Unclear/insufficient Crowdsourced/direct–upload/YouTube home–video dataset; public validation dataset with child_id mapping No known overlap
5 Grossi et al. (32) Italy 20/40 40 participants (20 ASD, 20 neuropsychiatric controls) Participant/EEG feature vector Pediatric Diagnosis/detection EEG Other/Unclear Other/Unclear Reviewer–selected best–performing Clearly defined Texas archive + prior Italian dataset No known overlap
6 Li et al. (33) China 136/272 272 children (136 ASD, 136 TD) Participant/video (1 per child) Pediatric Diagnosis/detection Eye–tracking/video–audio RNN/LSTM Cross–validation Author–designated primary/final Clearly defined Self–collected school–based raw–video dataset No known overlap
7 Bajestani et al. (34) Iran 30/60 60 participants (30 ASD, 30 controls) Participant; 1 selected EEG segment per participant Pediatric Diagnosis/detection EEG KNN Cross–validation Author–designated primary/final Unclear/insufficient Self–collected EEG dataset No known overlap
8 Zhao et al. (35) China 20/43 43 participants (20 ASD, 23 TD) Participant; repeated motor trials aggregated within participant Pediatric Diagnosis/detection Clinical/Behavioral KNN Cross–validation Reviewer–selected best–performing Clearly defined Self–collected Shenzhen pediatric cohort; restricted–kinematic motor task Probable overlap: Zhao series
9 Alcañiz Raya (36) Spain 10/20 92 participants across study phases; evaluation subset n=20 Participant Pediatric Diagnosis/detection Multimodal Support Vector Machine Hold–out validation Author–designated primary/final Clearly defined Self–collected electrodermal–activity + virtual–reality cohort No known overlap
10 Drimalla et al. (37) Germany 36/79 80 main–study participants; evaluation subset n=79 Participant; video/audio features aggregated per participant Adult/Mixed Diagnosis/detection Multimodal Random forest Cross–validation Author–designated primary/final Clearly defined Original simulated–interaction–task cohort No known overlap
11 Lai et al. (38) China 23/46 70 participants overall; matched evaluation cohort n=46 (23 ASD, 23 controls) Participant/retinal–image classification Pediatric Diagnosis/detection Imaging Support Vector Machine Cross–validation Single eligible model Clearly defined Self–collected retinal–image cohort No known overlap
12 Pham et al. (39) Singapore 40/77 77 participants (40 ASD, 37 controls) Participant; EEG segments used only for feature processing Pediatric Diagnosis/detection EEG Other/Unclear Cross–validation Author–designated primary/final Unclear/insufficient Self–collected EEG cohort No known overlap
13 Megerian et al. (40) USA 64/135 425 completers; evaluation subset n=135 Participant/child Pediatric Diagnosis/detection Multimodal Decision Tree External validation Single eligible model Clearly defined 14–site prospective cohort No known overlap
14 Cheng et al. (41) China 71/95 95 participants (71 ASD, 24 TD) Participant; multimodal behavior signals aggregated per child Pediatric Diagnosis/detection Multimodal Support Vector Machine Cross–validation Author–designated primary/final Clearly defined Self–collected multimodal behavior dataset No known overlap
15 Hendr et al. (42) Cyprus 10/21 104 participants; evaluation subset n=21 Participant; 18 handwriting tasks aggregated to one diagnosis Pediatric Diagnosis/detection Clinical/Behavioral CNN Cross–validation Author–designated primary/final Unclear/insufficient Author–collected handwriting/drawing dataset No known overlap
16 Thapa et al. (43) USA 2,795/7,393 36,965 participants in SPARK primary cohort; evaluation subset n=7,393 Participant; four–class output folded to ASD–spectrum vs non–spectrum Pediatric Diagnosis/detection Clinical/Behavioral Ensemble Hold–out validation Single eligible model Unclear/insufficient SPARK primary dataset; ABIDE supplementary dataset Potential overlap: SPARK
17 Wadhera (44) India 6/12 60 participants (30 ASD, 30 TD); evaluation subset n=12 Participant Unclear Diagnosis/detection Multimodal Support Vector Machine Hold–out validation Author–designated primary/final Unclear/insufficient Self–collected multimodal EEG + eye–tracking + behavioral dataset No known overlap
18 Zhao et al. (45) China 19/39 39 children (19 ASD, 20 TD) Child–level classification; gaze–behavior segments aggregated to child level Pediatric Diagnosis/detection Eye–tracking/video–audio Support Vector Machine Cross–validation Author–designated primary/final Clearly defined Shared Shenzhen pediatric face–to–face conversation cohort; eye–tracking/oculomotor data Shared cohort: Zhao series
19 Leroy et al. (46) USA 18/35 185 Arizona ADDM records; evaluation subset n=35 Child/case level; sentence predictions aggregated to one child result Pediatric Diagnosis/detection Clinical/Behavioral Ensemble Hold–out validation Author–designated primary/final Clearly defined Arizona ADDM records (2014, 2016) No known overlap
20 Luo et al. (47) China 20/45 45 participants (20 ASD, 25 controls) Participant; EEG windows used for feature extraction Pediatric Diagnosis/detection EEG Support Vector Machine Cross–validation Author–designated primary/final Clearly defined Institutional EEG cohort No known overlap
21 Natraj et al. (48) Switzerland 40/80 160 children (80 ASD, 80 TD); evaluation subset n=80 Participant/video; segment predictions aggregated to subject level Pediatric Diagnosis/detection Multimodal Ensemble Hold–out validation Author–designated primary/final Clearly defined Self–collected video–audio cohort No known overlap
22 Xie et al. (49) China 20/39 39 participants (20 ASD, 19 TD) Participant; multiple images per subject used for feature learning Adult/Mixed Diagnosis/detection Eye–tracking/video–audio CNN Cross–validation Single eligible model Clearly defined Previously established self–collected eye–tracking/visual–attention dataset No known overlap
23 Perochon et al. (50) USA 49/475 475 children (49 ASD, 426 non–ASD) Participant/child; video/gaze features aggregated Pediatric Diagnosis/detection Multimodal Ensemble Cross–validation Author–designated primary/final Unclear/insufficient Prospective clinical digital–behavioral–phenotyping cohort No known overlap
24 Rajagopalan et al. (27) Sweden 10,476/11,936 SPARK v8 development ≈30,660; external test n=11,936 newly recruited SPARK v10 participants Participant Adult/Mixed Diagnosis/detection Clinical/Behavioral Ensemble External validation Author–designated primary/final Unclear/insufficient SPARK v8 development; SPARK v10 new recruits for external test; additional SSC validation Potential overlap: SPARK
25 Ben–Sasson et al. (51) Israel 1,164/775,941 Source EHR cohort n=780,610; analyzed population n=775,941 (1,164 ASD, 774,777 non–ASD) Participant/longitudinal child EHR record Pediatric Diagnosis/detection Clinical/Behavioral Ensemble Cross–validation Author–designated primary/final Unclear/insufficient Maccabi Healthcare Services well–baby EHR No known overlap
26 Zhao et al. (28) China 20/41 41 children (20 ASD, 21 TD) Participant; whole–body movement features aggregated per child Pediatric Diagnosis/detection Eye–tracking/video–audio Support Vector Machine Cross–validation Author–designated primary/final Clearly defined Shared Shenzhen pediatric face–to–face conversation cohort; whole–body video data Shared cohort: Zhao series
ASD, autism spectrum disorder; CNN, convolutional neural network; EEG, electroencephalography; KNN, k–nearest neighbors; RNN/LSTM, recurrent neural network/long short–term memory; TD, typically developing; ADOS, Autism Diagnostic Observation Schedule; ADDM, Autism and Developmental Disabilities Monitoring. The participant-level 2 × 2 analytic sample is shown as ASD cases/total, calculated as TP + FN and TP + FN + FP + TN, respectively; the denominator therefore represents the participant-level evaluation N used in the meta-analysis. The participant-level cohort/sample-size column records the independent participant cohort reported for each study and may exceed the analytic sample when only a subset contributed to the selected 2 × 2 estimate. Unit of analysis specifies the level at which diagnostic classification was evaluated. Dataset source and overlap flag document potential non-independence across reports. ‘Potential overlap' denotes a dataset-level overlap concern without proof of duplicate participants; ‘Shared cohort' indicates clear reuse of the same underlying participant cohort; and ‘Probable overlap' indicates strong evidence of participant overlap without participant identifiers allowing exact matching. For the conservative dataset-independence sensitivity analysis, one representative estimate was retained per overlap cluster [ADOS repositories: Duda et al. (26); SPARK: Rajagopalan et al. (27); Zhao series: Zhao et al. (35)], yielding 21 studies. Model-selection strategy was classified as author-designated primary/final when the original authors prespecified or explicitly selected the main model/configuration for subsequent validation or reporting; reviewer-selected best-performing when multiple eligible models/configurations remained without a unique study-level main model and the review selected the best-performing eligible result; or single eligible model when only one model met the quantitative-synthesis criteria. Reference standard was classified as clearly defined or unclear/insufficient according to the review criteria used for the corresponding sensitivity analysis.
2.6Risk of bias and applicability assessment
Risk of bias and applicability concerns were assessed independently by two reviewers (QW and QHW) using a modified Quality Assessment of Diagnostic Accuracy Studies–Artificial Intelligence (QUADAS-AI) tool (25). Disagreements were resolved through discussion, with arbitration by a third reviewer (RL) when necessary. Although PROBAST was specified in the PROSPERO registration, a modified QUADAS-AI tool was adopted during review conduct because it was considered more appropriate for the diagnostic-accuracy focus of this review and allowed assessment of AI-specific methodological and applicability concerns. This change represented a deviation from the registered protocol.
The assessment covered four domains: patient selection, index test, reference standard, and flow and timing. Patient selection was evaluated with respect to the source and selection of participants, eligibility criteria, sampling approach, use of case-control designs, and the relevance and representativeness of the study population and setting to the review question. The index test domain considered the validation strategy, particularly whether external validation was performed, as well as data preprocessing and partitioning and whether model evaluation was adequately separated from model development, and whether model implementation and interpretation were appropriate for the review question. The reference standard domain addressed whether ASD and non-ASD status were established using an adequately defined diagnostic reference, while flow and timing concerned the interval between the index test and the reference standard. Overall judgments were made on the basis of the signaling questions within each domain. Applicability concerns were assessed separately for patient selection, index test, and reference standard. The modified QUADAS-AI tool was used to assess conventional sources of diagnostic-accuracy bias as well as AI-specific concerns related to data partitioning, model validation, implementation, and clinical applicability.
For the reference-standard sensitivity analysis, the reference standard was considered clearly defined when ASD status was established using recognized diagnostic criteria (e.g., DSM or ICD), standardized autism-specific diagnostic instruments (e.g., ADOS or ADI-R), diagnosis or confirmation by qualified clinicians, or an equivalent clearly documented diagnostic ascertainment procedure. Studies for which the basis of ASD case or control status was insufficiently described or could not be reliably established were classified as having an unclear or insufficiently defined reference standard. This classification was applied specifically to the sensitivity analysis and was separate from the overall QUADAS-AI risk-of-bias judgment for the reference-standard domain.
2.7Statistical analysis
Statistical analyses were performed using R version 4.3.2. Pooled sensitivity and specificity with 95% confidence intervals (CIs) were estimated using a bivariate Reitsma random-effects model fitted by restricted maximum likelihood, accounting for the correlation between the two measures. The random-effects framework was used to accommodate anticipated clinical and methodological heterogeneity across study populations, data modalities, algorithms, and validation strategies. Overall diagnostic performance was summarized using hierarchical summary receiver operating characteristic (HSROC) curves and corresponding AUC values. A continuity correction of 0.5 was applied to zero-cell studies when required.
The primary quantitative synthesis included one participant- or case-level diagnostic-accuracy estimate from each of 26 included studies, selected according to the threshold and model-selection rules described above. To assess the potential influence of non-independent datasets, a conservative dataset-independent sensitivity analysis was performed by retaining one estimate per identified overlap cluster, yielding 21 studies. The representative estimate retained from each identified overlap cluster is documented in Table 1. For the ADOS-repository cluster, Duda et al. (26) was retained because it represented a large subsequent validation sample drawn from multiple ADOS repositories. For the SPARK cluster, Rajagopalan et al. (27) was retained because its principal evaluation used a clearly defined external test cohort of newly recruited SPARK v10 participants. For the Shenzhen/Zhao-series cluster, Zhao et al. (35) was retained because it was the earliest eligible report in the series, used the complete 43-participant cohort, and provided participant-level cross-validation. To assess potential optimism associated with model selection, studies were classified as author-designated primary/final models, reviewer-selected best-performing models, or single eligible models, as described above. Because only three studies contributed reviewer-selected best-performing models, a formal bivariate comparison between model-selection groups was not performed. Sensitivity analyses were performed by excluding the three studies with reviewer-selected best-performing models and, separately, by restricting the analysis to studies with clearly defined reference standards. The overlap between reviewer-selected best-performing models and unclear or inadequate reference standards was examined descriptively.
Subgroup analyses were conducted by age group, validation strategy, data modality, and algorithm family. In addition to the quantitative subgroup analyses, a structured comparative narrative synthesis was conducted to examine differences in study population, data modality, algorithm family, validation strategy, use of external validation, and reported diagnostic performance. Because these methodological characteristics were interrelated and several subgroups included only a small number of studies, the comparisons were interpreted descriptively and not as evidence of independent effects attributable to individual methodological features. For each subgroup, pooled sensitivity and specificity were estimated using the same bivariate framework. HSROC AUCs for the overall analysis, subgroup analyses, and sensitivity analyses were accompanied by bias-corrected and accelerated (BCa) 95% CIs based on 5,000 study-level bootstrap replicates. Point AUC estimates were calculated from the Rutter–Gatsonis SROC curve derived from the original fitted Reitsma model using the AUC.reitsma method in the mada package. AUCs were not reported when the fitted SROC curve was considered unstable. For each bootstrap replicate, studies were resampled with replacement, the bivariate Reitsma model was refitted, and the HSROC AUC was recalculated using the same Rutter–Gatsonis SROC-based procedure as for the point estimate; the acceleration parameter for the BCa interval was estimated using leave-one-study-out jackknife resampling. For subgroup analyses, AUCs were not reported when the original fitted Reitsma model showed an unstable random-effects covariance structure, and BCa confidence intervals were not calculated in those cases. To avoid unstable pooled estimates from extremely sparse subgroups, subgroup-specific pooled estimates were not calculated for categories containing fewer than four studies; these categories were summarized descriptively.
Between-study heterogeneity in sensitivity and specificity was summarized using I2, τ2, and Cochran's Q P values. Potential sources of heterogeneity were examined using separate univariable bivariate random-effects meta-regression models within the Reitsma framework for age group, data modality, validation strategy, and broad algorithm class. Overall covariate effects were assessed by likelihood-ratio tests comparing maximum-likelihood models with and without the corresponding covariate, fitted to the same subset of studies. Coefficients and variance components were estimated using restricted maximum likelihood. Group-specific sensitivity and specificity estimates and 95% CIs were calculated as fixed-effect linear combinations from the full REML meta-regression models using the complete fixed-effect covariance matrix and back-transformed to the probability scale. Studies with unclear classifications or extremely sparse categories were excluded only from the corresponding meta-regression. Specifically, the single imaging study was excluded from the modality meta-regression but retained in the descriptive subgroup analysis. For the broad algorithm-class meta-regression, individual algorithm families were grouped into three categories: traditional non-ensemble machine-learning methods, ensemble methods, and deep neural networks. Changes in estimated random-effects variances relative to the corresponding intercept-only models were summarized descriptively. Metric-specific Wald tests and pairwise odds-ratio contrasts were considered exploratory secondary analyses and were not interpreted as diagnostic odds ratios. Multivariable and interaction models were not fitted because several cross-classified cells contained too few studies to permit stable estimation.
The primary synthesis was further assessed using leave-one-out sensitivity analysis. Each study was sequentially omitted, and the bivariate Reitsma random-effects model was refitted using the remaining 25 studies. The resulting pooled sensitivity and specificity estimates and their 95% CIs were compared with those obtained from the complete 26-study dataset. For each metric, the range of leave-one-out estimates and the largest absolute change from the full-data estimate were recorded.
Funnel-plot asymmetry was assessed using Deeks' test. The test was applied to the primary participant-level dataset (n = 26), the dataset-independent sensitivity dataset (n = 21), the dataset excluding reviewer-selected best-performing models (n = 23), and the dataset restricted to studies with clearly defined reference standards (n = 16). The direction of the regression slope was reported together with its statistical significance. A two-sided P < 0.05 was considered to indicate significant funnel-plot asymmetry.
3Results
3.1Study selection
A total of 17,387 records were identified through database searches, including PubMed (n = 3,220), Embase (n = 3,005), the Cochrane Library (n = 180), Web of Science (n = 8,330), and IEEE Xplore (n = 2,652). Before screening, 175 duplicate records were removed. The remaining 17,212 records underwent title and abstract screening, of which 17,110 were excluded.
The full texts of 102 reports were sought and successfully retrieved. All 102 reports were assessed for eligibility, of which 76 were excluded for the following reasons: outside the scope of the review (n = 28), insufficient diagnostic accuracy data to extract or reconstruct a 2 × 2 contingency table (n = 22), overlapping data (n = 7), unpublished conference abstracts (n = 5), diagnostic counts based on lower-level observations such as images, EEG segments, sessions, or raw samples (n = 6), inability to reliably reconstruct a unique participant-level 2 × 2 table from the reported validation results (n = 7), and a surveillance case-ascertainment task that did not meet the clinically oriented task criterion (n = 1). Consequently, 26 studies were included in the systematic review and primary quantitative synthesis. The study selection process is shown in Figure 1.
3.2Study characteristics
The main characteristics of the 26 studies included in the systematic review and meta-analysis are summarized in Table 1 (26–51). The studies were published between 2012 and 2025 and were conducted across multiple countries, with China (n = 8) and the United States (n = 8) contributing the largest numbers. One eligible diagnostic-accuracy estimate for binary ASD-versus-non-ASD classification was retained from each study. All 2 × 2 tables used in the primary analysis represented participant- or case-level classifications rather than image-, segment-, or trial-level observations. Where lower-level images, signal segments, repeated trials, or video segments were used for feature extraction or intermediate prediction, the retained diagnostic result was aggregated or evaluated at the participant level. Participant-level cohort size and the number of participants contributing to the selected 2 × 2 table are reported separately in Table 1 when these differed.
Regarding data modality, nine studies used clinical or behavioral data, five used eye-tracking or video/audio data, four used EEG data, one used imaging data, and seven used multimodal data. Most studies focused on pediatric populations: 21 included children or adolescents, four involved adult or mixed-age samples, and one had an unclear age classification. The included studies used a range of AI algorithms. Support vector machines were the most common (n = 8), followed by ensemble methods (n = 6), decision trees (n = 3), CNNs (n = 2), KNNs (n = 2), other or unclear algorithms (n = 2), random forests (n = 1), RNN/LSTM models (n = 1), and logistic regression (n = 1).
Regarding validation strategies, 15 studies used cross-validation, five used hold-out validation, five contributed externally validated diagnostic-accuracy estimates, and one used an other or unclear validation approach. Eighteen studies contributed estimates from models designated by the original authors as the primary, final, or main model, three contributed reviewer-selected best-performing models, and five had only one eligible model. Sixteen studies had clearly defined reference standards according to the operational criteria used for the reference-standard sensitivity analysis, whereas ten were classified as unclear or insufficiently defined.
Potential non-independence of data sources was identified across three groups of reports: three studies drew on overlapping ADOS repositories, two used SPARK data, and three were based on the same or probably overlapping Shenzhen cohort. These relationships are documented in Table 1. A conservative dataset-independent sensitivity analysis retaining one estimate per overlap cluster was therefore based on 21 studies. Overall, the evidence base remained predominantly pediatric and internally validated, with relatively limited evaluation in independent external datasets.
3.3Risk of bias and applicability concerns
Risk of bias and applicability concerns were assessed across the 26 included studies using the modified QUADAS-AI tool. Risk of bias was evaluated across four domains: patient selection, index test, reference standard, and flow and timing. Applicability concerns were evaluated across three domains: patient selection, index test, and reference standard. The summary of judgments is presented in Figure 2.
3.3.1Risk of bias
Methodological concerns were most frequent in the patient selection and index test domains. In the patient selection domain, 23 studies were rated as high risk (88.5%) and three as low risk (11.5%). In the index test domain, 18 studies were rated as high risk (69.2%) and eight as low risk (30.8%). High-risk judgments in these domains were mainly related to selected or convenience samples, case-control designs, narrowly defined study populations, and the lack of independent model evaluation.
In the reference standard domain, three studies were rated as high risk (11.5%), eight as unclear risk (30.8%), and 15 as low risk (57.7%). Unclear or high-risk judgments were mainly related to incomplete reporting of the diagnostic procedure or insufficiently defined non-ASD reference labels. In the flow and timing domain, 17 studies were rated as unclear risk (65.4%) and nine as low risk (34.6%), with no study rated as high risk. The unclear judgments were mainly related to insufficient reporting of the interval between the reference diagnosis and the AI-based assessment (Figure 2).
3.3.2Applicability concerns
Applicability concerns were mainly related to patient selection. In the patient selection domain, 21 studies were rated as high concern (80.8%) and five as low concern (19.2%), with no study rated as unclear. The high applicability concerns were largely related to the use of selected or convenience samples, case-control designs, narrowly defined study populations, and comparison groups that may not fully represent the broader clinical populations in which ASD detection models would ultimately be applied.
Applicability concerns were minimal in the index test domain, with all 26 studies rated as low concern (100.0%). In the reference standard domain, three studies were rated as high concern (11.5%), eight as unclear concern (30.8%), and 15 as low concern (57.7%). Unclear or high applicability concerns were mainly associated with insufficiently documented diagnostic procedures or reference labels that did not fully correspond to a clearly established clinical diagnosis (Figure 2).
3.3.3Overall assessment
Overall, the modified QUADAS-AI assessment identified patient selection and model evaluation as the main methodological limitations of the available evidence, with additional concerns related to incomplete reporting of reference standards and flow and timing.
3.4Overall diagnostic performance
In the primary participant-level analysis of 26 studies using the bivariate Reitsma random-effects model, pooled sensitivity was 0.908 (95% CI: 0.861–0.940; Figure 3A) and pooled specificity was 0.868 (95% CI: 0.830–0.898; Figure 3B). The corresponding HSROC AUC was 0.936 (BCa 95% CI: 0.860–0.973; Figure 4). Substantial heterogeneity was observed for both sensitivity (I2 = 96.7%; τ2 = 1.05; P < 0.001) and specificity (I2 = 95.8%; τ2 = 0.30; P < 0.001).
3.5Sensitivity analyses related to dataset overlap, model selection, and reference standards
To examine the potential influence of non-independent datasets, the analysis was repeated after retaining one representative estimate per identified overlap cluster. This dataset-independent analysis included 21 studies and yielded a pooled sensitivity of 0.870 (95% CI: 0.820–0.908), pooled specificity of 0.841 (95% CI: 0.813–0.865), and an HSROC AUC of 0.900 (BCa 95% CI: 0.813–0.956; Figure 5). Compared with the primary 26-study analysis, pooled sensitivity decreased from 0.908 to 0.870, pooled specificity from 0.868 to 0.841, and the HSROC AUC from 0.936 to 0.900.
Among the 26 studies in the primary analysis, 18 contributed estimates from models designated by the original authors as primary, final, or main models, three contributed reviewer-selected best-performing models because no primary or final model had been specified, and five reported a single eligible model. Given the small number of studies in the reviewer-selected group, a formal bivariate comparison between model-selection strategies was not performed. After excluding the three studies with reviewer-selected best-performing models, the remaining 23 studies had a pooled sensitivity of 0.901 (95% CI: 0.848–0.937), pooled specificity of 0.829 (95% CI: 0.814–0.844), and an HSROC AUC of 0.867 (BCa 95% CI: 0.804–0.936; Supplementary Figure S1). Relative to the primary analysis, pooled sensitivity decreased from 0.908 to 0.901, pooled specificity from 0.868 to 0.829, and the HSROC AUC from 0.936 to 0.867, with the largest attenuation observed for AUC.
When the analysis was restricted to the 16 studies with clearly defined reference standards, pooled sensitivity was 0.910 (95% CI: 0.852–0.946), pooled specificity was 0.903 (95% CI: 0.854–0.937), and the HSROC AUC was 0.957 (BCa 95% CI: 0.911–0.980; Supplementary Figure S2). Compared with the primary analysis, sensitivity, specificity, and AUC changed by +0.002, +0.035, and +0.021, respectively. Restricting the synthesis to studies with clearly defined reference standards therefore did not reduce the pooled diagnostic-performance estimates.
3.6Subgroup analyses
Subgroup analyses were performed according to age group, validation strategy, data modality, and algorithm family. Pooled sensitivity and specificity varied numerically across the estimable subgroups, and these differences were further examined using meta-regression. HSROC AUCs were reported only for subgroups in which the SROC fit was considered sufficiently stable; subgroups with fewer than four studies were described rather than pooled. The subgroup results are summarized in Table 2, and forest plots of pooled sensitivity and specificity are provided in Supplementary Figures S3–S6.
Table 2Subgroup analyses of pooled diagnostic performance of artificial intelligence models for autism spectrum disorder detection.
Subgroup domain Subgroup Studies, n Pooled sensitivity (95% CI) Pooled specificity (95% CI) HSROC AUC (BCa 95% CI)
Age group Pediatric 21 0.911 (0.865–0.942) 0.875 (0.833–0.908) 0.945 (0.859–0.973)
Adult/Mixed 4 0.953 (0.556–0.997) 0.858 (0.737–0.928) Not reported*
Unclear 1 Not pooled Not pooled Not pooled
Validation strategy Cross–validation 15 0.888 (0.820–0.932) 0.884 (0.847–0.914) Not reported*
Hold–out validation 5 0.878 (0.688–0.959) 0.886 (0.867–0.903) Not reported*
External validation 5 0.940 (0.848–0.978) 0.856 (0.712–0.934) 0.956 (0.792–0.982)
Other/Unclear 1 Not pooled Not pooled Not pooled
Data modality Clinical/Behavioral 9 0.934 (0.833–0.976) 0.889 (0.815–0.935) 0.953 (0.858–0.986)
Eye–tracking/Video–Audio 5 0.910 (0.860–0.944) 0.878 (0.765–0.941) Not reported*
EEG 4 0.939 (0.821–0.981) 0.937 (0.801–0.982) Not reported*
Multimodal 7 0.835 (0.724–0.906) 0.807 (0.773–0.837) Not reported*
Imaging 1 Not pooled Not pooled Not pooled
Algorithm family Support Vector Machine 8 0.922 (0.854–0.959) 0.909 (0.828–0.954) Not reported*
Ensemble 6 0.857 (0.707–0.937) 0.820 (0.798–0.840) 0.850 (0.746–0.866)
Decision Tree 3 Not pooled Not pooled Not pooled
CNN 2 Not pooled Not pooled Not pooled
KNN 2 Not pooled Not pooled Not pooled
Other/Unclear 2 Not pooled Not pooled Not pooled
Random Forest 1 Not pooled Not pooled Not pooled
RNN/LSTM 1 Not pooled Not pooled Not pooled
Logistic Regression 1 Not pooled Not pooled Not pooled
Pooled sensitivity and specificity are presented as proportions with 95% confidence intervals and rounded to three decimals; HSROC AUC values are presented with BCa 95% confidence intervals and rounded to three decimals. Categories containing fewer than four studies were summarized descriptively and were not pooled. *AUC was not reported when the fitted SROC curve or random–effects covariance structure was unstable. AUC, area under the curve; BCa, bias-corrected and accelerated; HSROC, hierarchical summary receiver operating characteristic; EEG, electroencephalography; RNN, recurrent neural network; LSTM, long short-term memory; KNN, k-nearest neighbors; CNN, convolutional neural network.
3.6.1Age group
The pediatric subgroup included 21 studies, with a pooled sensitivity of 0.911 (95% CI: 0.865–0.942) and a pooled specificity of 0.875 (95% CI: 0.833–0.908; Supplementary Figures S3A, B). The corresponding HSROC AUC was 0.945 (BCa 95% CI: 0.859–0.973).
Four studies were included in the adult/mixed-age subgroup, with a pooled sensitivity of 0.953 (95% CI: 0.556–0.997) and a pooled specificity of 0.858 (95% CI: 0.737–0.928). The wide confidence interval for sensitivity reflected the small number of studies in this subgroup. Because the fitted SROC was unstable, an AUC was not reported for the adult/mixed-age subgroup. One study was classified in the unclear-age subgroup and was therefore described without pooling. Meta-regression showed no significant overall association between age group and diagnostic performance (P = 0.879; Section 3.7).
3.6.2Validation strategy
Among studies using cross-validation (n = 15), pooled sensitivity was 0.888 (95% CI: 0.820–0.932) and pooled specificity was 0.884 (95% CI: 0.847–0.914; Supplementary Figures S4A, B). For hold-out validation (n = 5), the corresponding estimates were 0.878 (95% CI: 0.688–0.959) and 0.886 (95% CI: 0.867–0.903), respectively. Among the five studies contributing externally validated estimates, pooled sensitivity was 0.940 (95% CI: 0.848–0.978) and pooled specificity was 0.856 (95% CI: 0.712–0.934). One study was classified as having an other or unclear validation strategy and was not pooled.
The HSROC AUC for the external-validation subgroup was 0.956 (BCa 95% CI: 0.792–0.982). AUCs were not reported for the cross-validation or hold-out subgroups because their fitted SROC shapes were unstable. Meta-regression showed no significant overall association between validation strategy and diagnostic performance (P = 0.181; Section 3.7).
3.6.3Data modality
Among the nine studies using clinical or behavioral data, pooled sensitivity was 0.934 (95% CI: 0.833–0.976) and pooled specificity was 0.889 (95% CI: 0.815–0.935; Supplementary Figures S5A, B). The corresponding HSROC AUC was 0.953 (BCa 95% CI: 0.858–0.986).
For eye-tracking or video/audio data (n = 5), pooled sensitivity was 0.910 (95% CI: 0.860–0.944) and pooled specificity was 0.878 (95% CI: 0.765–0.941). Four studies used EEG data, with a pooled sensitivity of 0.939 (95% CI: 0.821–0.981) and pooled specificity of 0.937 (95% CI: 0.801–0.982). Seven studies used multimodal data, with corresponding estimates of 0.835 (95% CI: 0.724–0.906) and 0.807 (95% CI: 0.773–0.837), respectively. AUCs were not reported for these three subgroups because the fitted SROC shapes were unstable. The imaging subgroup included only one study and was therefore described without pooling. Meta-regression showed no significant overall association between data modality and diagnostic performance (P = 0.739; Section 3.7).
3.6.4Algorithm family
Subgroup analysis by algorithm family showed numerical variation in pooled diagnostic estimates (Supplementary Figures S6A, B). Eight studies used support vector machines, with a pooled sensitivity of 0.922 (95% CI: 0.854–0.959) and pooled specificity of 0.909 (95% CI: 0.828–0.954). Six studies used ensemble methods, with a pooled sensitivity of 0.857 (95% CI: 0.707–0.937) and pooled specificity of 0.820 (95% CI: 0.798–0.840).
The HSROC AUC for the ensemble subgroup was 0.850 (BCa 95% CI: 0.746–0.866). An AUC was not reported for the support vector machine subgroup because the fitted SROC was unstable. No pooled estimates were calculated for decision trees, CNNs, KNNs, logistic regression, random forests, RNN/LSTM, or other/unclear algorithms because each category included fewer than four studies. Broad algorithm class showed a significant overall association with diagnostic performance in meta-regression (P = 0.030; Section 3.7), although individual group contrasts were interpreted cautiously.
The unstable fitted SROC curves for the adult/mixed-age, cross-validation, hold-out validation, eye-tracking/video-audio, EEG, multimodal, and support vector machine subgroups are shown in Supplementary Figures S7A–G.
3.7Meta-regression analyses of heterogeneity
Separate univariable bivariate random-effects meta-regression models within the Reitsma framework showed no significant overall association of diagnostic performance with age group (n = 25; likelihood-ratio χ2 = 0.257, df = 2, P = 0.879), data modality (n = 25; χ2 = 3.535, df = 6, P = 0.739), or validation strategy (n = 25; χ2 = 6.248, df = 4, P = 0.181; Figure 6).
Broad algorithm class showed a significant overall association with diagnostic performance (n = 24; χ2 = 10.687, df = 4, P = 0.030). The analysis included 14 studies using traditional non-ensemble machine-learning methods, seven using ensemble methods, and three using deep neural networks; two studies classified as other/unclear were excluded. Model-derived sensitivity and specificity estimates were 0.930 (95% CI: 0.876–0.961) and 0.869 (95% CI: 0.818–0.908), respectively, for traditional non-ensemble machine learning; 0.838 (95% CI: 0.708–0.918) and 0.820 (95% CI: 0.763–0.866) for ensemble methods; and 0.898 (95% CI: 0.686–0.973) and 0.920 (95% CI: 0.837–0.963) for deep neural networks.
However, exploratory metric-specific Wald tests were not statistically significant for sensitivity (P = 0.179) or false-positive rate (P = 0.078), and none of the pairwise sensitivity or specificity contrasts relative to traditional non-ensemble machine learning reached statistical significance (Supplementary Figure S8). Inclusion of broad algorithm class was associated with descriptive reductions of 7.3% and 35.2% in the estimated random-effects variances on the logit-sensitivity and logit false-positive-rate scales, respectively. The single imaging study was retained in the descriptive subgroup analysis but excluded from the modality meta-regression. Because the deep-neural-network subgroup contained only three studies and several cross-classified cells were sparse, these study-level associations were interpreted cautiously.
3.8Leave-one-out sensitivity analysis
Leave-one-out sensitivity analysis showed that the pooled diagnostic estimates were generally stable after sequential omission of individual studies (Supplementary Figure S9). Across the 26 leave-one-out analyses, pooled sensitivity ranged from 0.894 to 0.913, compared with 0.908 (95% CI: 0.861–0.940) in the primary analysis. The largest absolute change in pooled sensitivity occurred when Thapa et al. (43) was omitted, yielding 0.894 (95% CI: 0.848–0.928), compared with 0.908 in the primary analysis.
Pooled specificity ranged from 0.830 to 0.875, compared with 0.868 (95% CI: 0.830–0.898) in the primary analysis. The largest absolute change occurred when Kosmicki et al. (30) was omitted, yielding a pooled specificity of 0.830 (95% CI: 0.815–0.844), an absolute change of 0.038. Overall, the pooled estimates were relatively stable to the omission of individual studies, although specificity showed greater sensitivity to individual-study omission than sensitivity.
3.9Funnel-plot asymmetry
Deeks' test showed no significant funnel-plot asymmetry in the primary 26-study participant-level analysis (slope = 7.820, t = 0.678, df = 24, P = 0.504; Figure 7A). The slope was positive, indicating that smaller studies tended to have higher diagnostic odds ratios (DORs), although this pattern was not statistically significant.
In the dataset-independent analysis of 21 studies, the slope remained positive and funnel-plot asymmetry was statistically significant (slope = 16.066, t = 4.206, df = 19, P < 0.001; Figure 7B), with smaller studies tending to report higher DORs. No significant asymmetry was observed after excluding the three studies with reviewer-selected best-performing models (n = 23; slope = 5.441, t = 0.453, df = 21, P = 0.655; Figure 7C), although the slope remained positive.
Among the 16 studies with clearly defined reference standards, the slope was negative (slope = −16.781, t = −1.925, df = 14, P = 0.075; Figure 7D), indicating that smaller studies tended to have lower rather than higher DORs. Overall, the direction and statistical significance of funnel-plot asymmetry varied across the different analysis sets, providing no consistent evidence of conventional small-study effects across analyses.
4Discussion
The primary participant-level meta-analysis of AI-assisted approaches for ASD detection suggested relatively high diagnostic performance in research settings. These findings, however, should not be interpreted as evidence of consistent performance across clinical settings. Between-study heterogeneity remained very high, external validation was uncommon, and concerns remained regarding risk of bias, applicability, model selection, the quality and reporting of reference standards, and potential non-independence of underlying datasets. Sensitivity analyses showed some attenuation of pooled performance after retaining one estimate per overlapping dataset and after excluding reviewer-selected best-performing models, whereas restricting the analysis to studies with clearly defined reference standards did not reduce the diagnostic-performance estimates. Funnel-plot asymmetry was not significant in the primary participant-level analysis and varied in both direction and statistical significance across sensitivity analyses, precluding a consistent interpretation as evidence of conventional small-study effects or selective reporting. In addition, the evidence base was dominated by pediatric populations and internally validated models, limiting confidence in generalizability to broader clinical populations and independent settings. Taken together, the available evidence suggests that AI may have value as an adjunct to established ASD assessment pathways, particularly for screening, referral support, and clinical decision-making, but does not yet support its use as a standalone diagnostic system (52–55).
Pediatric populations dominated the evidence base. However, meta-regression showed no significant association between age group and diagnostic performance, providing no evidence that performance was systematically better in pediatric populations. Although the adult/mixed-age subgroup showed numerically high sensitivity, the estimate was imprecise and the fitted SROC was unstable because few studies were available. Evidence in adult and mixed-age populations therefore remains limited, and population-specific validation is needed before models developed mainly in pediatric samples can be generalized to older populations (53, 54).
Validation strategy is important when considering the clinical relevance and transportability of reported diagnostic performance. Most included studies relied on internal validation, whereas external validation remained limited. Although externally validated models showed numerical differences in sensitivity and specificity, meta-regression did not show a significant association between validation strategy and diagnostic performance, and these differences should not be interpreted as evidence that one validation approach is superior. Instead, the limited external-validation evidence leaves uncertainty about whether model performance can be maintained across independent populations, institutions, acquisition settings, and clinical workflows. Consistent with this concern, a meta-analysis specifically of home-video-based machine-learning approaches reported lower pooled sensitivity and specificity in validation cohorts than in cross-validation analyses, further highlighting the importance of independent validation before clinical translation (56). Future studies should prioritize prospective, multicenter external validation using locked models and prespecified operating thresholds, with reporting guided by TRIPOD+AI and STARD-AI and methodological appraisal supported by PROBAST+AI (57–59).
Diagnostic performance varied numerically across data modalities, with EEG-based studies showing the highest pooled sensitivity and specificity among the estimable modality subgroups, whereas multimodal studies showed numerically lower pooled estimates. However, meta-regression showed no significant association between data modality and diagnostic performance, so these differences should not be interpreted as evidence of inherent superiority of any modality. Stable HSROC AUC estimates could not be obtained for several modality subgroups, further limiting direct comparisons. Observed differences may also reflect variation in participant characteristics, preprocessing, feature extraction, validation strategy, and clinical setting rather than modality alone. The imaging subgroup included only one study and was therefore summarized descriptively. The relatively lower performance of multimodal studies should be interpreted cautiously and may depend on data completeness, fusion strategy, model complexity, and validation design.
These findings should also be considered in relation to previous systematic reviews. A recent systematic review and meta-analysis focusing on AI-based analysis of facial and social-behavioral information for ASD assessment also reported promising diagnostic performance, while emphasizing the need for further validation in diverse populations (60). Compared with the broader review by Valizadeh et al. (61), our review used a more restrictive diagnostic-accuracy framework, requiring participant- or case-level data sufficient to construct or reconstruct a binary ASD-versus-non-ASD 2 × 2 table and retaining one eligible diagnostic estimate per included study. Valizadeh et al. synthesized results by modality using the Split Component Synthesis approach and assessed risk of bias with an adapted QUADAS-2 tool. In contrast, we jointly analyzed sensitivity and specificity using a bivariate Reitsma/HSROC framework and assessed study quality using a modified QUADAS-AI tool. We also evaluated dataset non-independence, model selection, reference-standard quality, heterogeneity, and the influence of individual studies through sensitivity analyses and meta-regression. Together, these methodological features allowed a more focused assessment of the robustness and generalizability of AI-assisted ASD diagnostic performance.
Diagnostic performance varied across algorithm families, and broad algorithm class showed an overall association with diagnostic performance in meta-regression. However, exploratory metric-specific tests and pairwise contrasts did not identify significant differences between individual algorithm classes, and substantial residual heterogeneity remained. Given the small number of deep-neural-network studies and potential confounding by data modality, sample characteristics, and validation design, these findings suggest that algorithm class may contribute to between-study heterogeneity but do not establish the superiority of any specific approach.
Sensitivity analyses provided additional context for interpreting the pooled estimates. Retaining one representative estimate per identified overlap cluster led to modest attenuation of pooled performance, suggesting that dataset overlap may contribute some optimism to study-level estimates. Excluding reviewer-selected best-performing models also reduced performance, particularly for specificity and AUC, although this finding should be interpreted cautiously because few studies required review-level model selection. By contrast, restricting the analysis to studies with clearly defined reference standards did not reduce pooled performance, suggesting that the primary findings were not driven by studies with unclear or insufficiently defined reference standards. Together, these analyses underscore the importance of dataset independence, prespecified or author-designated models, and clearly defined reference standards in future evaluations of AI-assisted ASD detection.
The modified QUADAS-AI assessment identified substantial methodological limitations, particularly in patient selection and index-test evaluation, with additional concerns regarding reference standards and flow and timing. Applicability concerns were concentrated in patient selection, as many studies relied on convenience samples, case-control designs, narrowly defined populations, or comparison groups that may not reflect broader clinical settings. Consequently, performance observed in comparisons between ASD cases and typically developing controls may not generalize to clinically relevant differential-diagnostic populations, particularly when independent model evaluation is lacking. These findings underscore the need for representative sampling, clinically appropriate comparison groups, and independent model evaluation before broader clinical application (25).
Leave-one-out analysis showed that the pooled estimates were generally stable, although specificity was more sensitive to individual-study omission. This numerical stability, however, does not address methodological limitations shared across studies. Funnel-plot asymmetry was not statistically significant in the primary participant-level analysis and varied in both direction and statistical significance across the sensitivity analyses. Although significant positive asymmetry was observed in the dataset-independent analysis, the remaining analyses were not statistically significant, and the reference-standard-restricted analysis showed a negative slope. These inconsistent patterns do not support a consistent interpretation of conventional small-study effects or selective reporting and should therefore be interpreted cautiously.
Several evidence gaps need to be addressed before AI-assisted ASD detection can be considered for routine clinical use. Future studies should enroll representative and clinically heterogeneous populations, including adults, use clearly defined reference diagnoses and clinically relevant comparison groups, and ensure strict participant-level separation of model development, tuning, and testing. Diagnostic performance should be evaluated at the participant or case level rather than treating repeated images, signal segments, or trials from the same individual as independent observations, and evaluation datasets should be independent of model-development data and, where possible, independent of datasets used in previous studies. Prospective multicenter external validation using locked models and prespecified operating thresholds should be prioritized to assess transportability across clinical settings. Evaluation should also extend beyond discrimination to calibration, clinical utility, fairness, interpretability, and implementation feasibility. These priorities are consistent with recent consensus guidance for trustworthy healthcare AI (62).
This review has several strengths, including the use of a bivariate diagnostic-accuracy framework, modified QUADAS-AI, and formal meta-regression. The synthesis was restricted to participant- or case-level diagnostic classifications, with targeted sensitivity analyses addressing dataset non-independence, model selection, and reference-standard quality. HSROC AUC uncertainty was assessed using BCa bootstrap confidence intervals, and AUCs were withheld when fitted SROC curves were unstable. Together, these approaches allowed a more robust assessment of diagnostic performance and the reliability of the underlying evidence.
5Conclusion
AI-assisted approaches show promising diagnostic performance for ASD detection, but the current evidence is not yet sufficiently robust to support broad clinical implementation. Substantial heterogeneity, methodological limitations, potential non-independence of underlying datasets, limited external validation, and the predominance of pediatric and internally validated studies constrain the generalizability of the reported performance. Findings across data modalities and algorithm classes should therefore be interpreted with caution.
At present, AI is better positioned as an adjunct to established ASD screening and diagnostic pathways than as a standalone diagnostic tool. Further progress will require prospective multicenter validation in representative clinical populations, participant-level evaluation, clearly defined reference diagnoses, prespecified models and operating thresholds, and independent datasets and evaluation procedures. Future studies should also assess calibration, clinical utility, fairness, interpretability, and implementation feasibility to determine whether diagnostic performance can translate into meaningful clinical benefit.
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Qian Wang, Rong Luo, Qianhui Wen. (2026). Artificial intelligence for detecting autism spectrum disorder: a systematic review and meta-analysis.. Frontiers in public health. DOI: 10.3389/fpubh.2026.1923851
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