This study adhered to the PRISMA-DTA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses of Diagnostic Test Accuracy) guidelines and was prospectively registered on PROSPERO (ID: CRD42023449927) to ensure transparency and minimize reporting bias [16,17]. Two reviewers independently conducted all stages of the review process, including title and abstract screening, full-text evaluation, data extraction, adherence assessment to reporting guidelines, and risk-of-bias evaluation. Discrepancies were resolved through group consensus.

Two investigators (TLZ and BW) systematically searched PubMed, Web of Science, and Embase from inception to January 2025 using a combination of Medical Subject Headings (MeSH) terms and free-text keywords. Additional searches were performed on clinical trial registries and OpenGrey to identify unpublished clinical trials and gray literature. Search terms encompassed four domains: (1) disease terminology (Alzheimer disease, AD, Alzheimer Syndrome); (2) imaging modalities (¹⁸F-FDG PET, sMRI); (3) AI methodologies (ML, DL); and (4) diagnostic metrics (sensitivity, specificity, summary receiver operating characteristic curve area [SROC-AUC]). Reference lists of included studies were manually screened to identify additional relevant publications. The specific search strategies are provided in Table S1 in Multimedia Appendix 1.

The inclusion criteria were as follows: (1) human studies developing or validating AI models using ¹⁸F-FDG PET or sMRI to differentiate AD from normal controls; (2) AD diagnosis based on National Institute on Aging-Alzheimer's Association or International Working Group for New Research Criteria for Alzheimer’s Disease criteria; (3) availability of diagnostic performance metrics (eg, true positives, false positives, true negatives, false negatives) or explicit reporting of sensitivity and specificity; and (4) full-text availability in English. The exclusion criteria were as follows: (1) case reports, reviews, letters, or conference abstracts; (2) studies lacking sufficient diagnostic performance data; and (3) duplicate publications reporting on the same cohort without novel analyses.

Two reviewers (TZ and BW) independently performed title and abstract and full-text screening, followed by cross-verification to ensure accuracy. Two additional investigators (RM and XH) extracted data using predefined forms, including study characteristics (first author, publication year), model specifications (algorithm type, validation strategies), and diagnostic performance metrics (2×2 contingency tables, sensitivity, specificity). Extracted data were cross-checked for completeness and precision.

The methodological quality of included studies was evaluated using an adapted TRIPOD-AI (Transparent Reporting of a Multivariable Prediction Model for Individual Prognosis or Diagnosis–Artificial Intelligence) checklist (Table S2 in Multimedia Appendix 1) by two independent reviewers (RM and XH) [18]. The instrument assessed four domains: (1) data quality (sample diversity, adequacy, preprocessing standardization), (2) model development (feature extraction rationale, algorithm selection, hyperparameter optimization), (3) validation methods (cross-validation rigor, external validation), and (4) clinical applicability (interpretability, net clinical benefit). Each of the nine items was scored 0‐2 (0=unsatisfied; 1=partially satisfied; 2=fully satisfied), with total scores categorized as high quality (≥16), moderate quality (10-15), or low quality (≤9). Disagreements were resolved through discussion.

Diagnostic performance metrics were calculated using a bivariate mixed-effects model. SROC-AUC served as the primary outcome due to its threshold independence. Diagnostic accuracy was classified per National Institutes of Health criteria as high (AUC≥0.90), moderate (0.70‐0.89), or low (AUC<0.70) [19].

Heterogeneity was quantified using Cochran Q test (significance defined at the .05 level) and I² statistics (25%: low; 50%: moderate; 75%: high heterogeneity) [20]. Threshold effects were assessed using Spearman correlation between logit-transformed sensitivity and 1–specificity. Sensitivity analyses evaluated outlier influence by iteratively excluding individual studies. Univariable meta-regression analyses were conducted to assess the influence of potential confounding factors, including study quality (moderate to high vs low quality), algorithm type (ML vs DL), and validation strategy (internal vs external validation). Statistical significance of modifiers of the pooled effect size was defined at the .05 level after adjustment via the Holm-Bonferroni method. Publication bias was assessed via funnel plot asymmetry and Egger test, with significance defined at the .05 level. All analyses were conducted in Stata 16.0 using the MIDAS commands.

As this study focused on diagnostic accuracy, we employed the bivariate random-effects model via the MIDAS command in Stata to jointly synthesize sensitivity and specificity. This approach accounts for both within- and between-study variability, as well as the inherent correlation between sensitivity and specificity. In such models, conventional heterogeneity measures like I², although still reported for completeness, may not fully capture the joint variability of test performance measures. Therefore, to better understand heterogeneity, we additionally performed meta-regression and calculated joint likelihood ratio tests to explore potential effect modifiers. These methods align with recommended practices in diagnostic test accuracy meta-analyses [21,22].

Initial searches identified 876 PubMed records (n=89 involving ¹⁸F-FDG PET; n=787 sMRI), 932 Embase records (n=111 ¹⁸F-FDG PET; n=821 sMRI), and 2610 Web of Science records (n=230 ¹⁸F-FDG PET; n=2380 sMRI), supplemented by 3 additional studies. After deduplication in EndNote 20, 2 reviewers independently screened titles and abstracts using the Population, Intervention, Comparison, Outcome, Study Design (PICOS) criteria, followed by full-text evaluation against predefined inclusion/exclusion criteria. This rigorous process yielded 38 studies for systematic review and meta-analysis [23-60]. The literature screening process and results are shown in Figure 1.

Table 1 and Table S3 in Multimedia Appendix 1 detail the characteristics of the included studies. Imaging modalities comprised sMRI (n=15, 39%), ¹⁸F-FDG PET (n=15, 39%), and combined sMRI/¹⁸F-FDG PET (n=8, 22%). Data sources predominantly relied on open-access databases (n=29, 76%), with 28 (97%) from the Alzheimer’s Disease Neuroimaging Initiative database and 1 (3%) from the Open Access Series of Imaging Studies database. Four studies (11%) used institutional data, while 5 (13%) combined Alzheimer’s Disease Neuroimaging Initiative database with local datasets. Algorithmically, 26 studies (68%) employed ML, predominantly support vector machines (17/26, 65%), whereas 12 (32%) utilized DL, primarily convolutional neural networks (9/12, 75%). Internal validation was implemented in 33 studies (87%), with 10-fold cross-validation in 16 (48%); only 5 studies (13%) incorporated external validation.

Nine (24%) studies were high quality, characterized by adequate sample sizes, rigorous validation (eg, multicenter external validation), and standardized reporting. Moderate-quality studies (n=19, 50%) met basic methodological standards (eg, cross-validation) but had limitations such as single-center data or insufficient clinical correlation analyses. Ten (26%) studies were low quality due to small sample sizes (<100 cases) and inadequate validation strategies, compromising external validity. The results of quality assessments for each study are detailed in Table S4 in Multimedia Appendix 1.

Funnel plot analysis of the full study cohort revealed no significant publication bias for sMRI (P=.69), whereas the ¹⁸F-FDG PET subgroup exhibited significant bias (P<.001). In the moderate-to-high-quality cohort, both sMRI (P=.03) and ¹⁸F-FDG PET (P=.01) demonstrated publication bias. However, subgroup analyses showed no significant bias for sMRI+ML (P=.06), sMRI+DL (P=.89), ¹⁸F-FDG PET+ML (P=.08), or ¹⁸F-FDG PET+DL (P=.28).

This meta-analysis confirms that AI-enhanced sMRI and ¹⁸F-FDG PET achieve high diagnostic accuracy for AD, with pooled SROC-AUCs of 0.94 and 0.96, respectively, outperforming conventional visual assessments [61,62]. ¹⁸F-FDG PET demonstrated superior overall performance (P=.02), likely attributable to its sensitivity to AD-specific metabolic abnormalities. Notably, ML amplified PET’s diagnostic advantage (SROC-AUC: 0.95 vs 0.89), while DL narrowed the gap (SROC-AUC: 0.97 vs 0.96), highlighting DL’s capacity to extract complex metabolic features and mitigate structural imaging limitations [63].

Subgroup analyses identified three key determinants of heterogeneity and performance variation. First, methodological quality significantly influenced sMRI models: moderate-to-high-quality studies reported lower sensitivity (87% vs 91%) and specificity (91% vs 95%) compared to low-quality studies (P=.02), suggesting inflated performance in the latter due to small sample sizes, single-center data, or nonstandardized preprocessing. Adherence to TRIPOD-AI guidelines and transparent reporting of preprocessing workflows are critical for future studies [18]. Second, algorithm type drove technical divergence in PET models: DL outperformed ML (sensitivity: 91% vs 89%; specificity: 94% vs 91%; P=.01) through end-to-end feature learning. However, ML’s interpretability better aligns with clinical demands for transparency, whereas DL’s reliance on large annotated datasets and computing resources limits its deployment in resource-constrained regions [64]. Third, validation strategies exposed generalizability limitations: external validation of sMRI+DL models showed reduced sensitivity (85% vs 90%) and specificity (91% vs 93%) compared to internal validation (P<.001).

The reduced diagnostic accuracy observed in externally validated models may stem from (1) data distribution shift—differences in feature distributions, class balance, and temporal trends between training and external datasets; (2) overfitting—models may have overfitted to training-specific noise or spurious patterns, limiting generalization; and (3) implementation and annotation inconsistencies—variations in data preprocessing, feature scaling, and labeling protocols across datasets [65].

This study has two methodological constraints: potential selection bias from English-only inclusion and possible overestimation by prioritizing optimal contingency tables. Future research should focus on enhancing evidence robustness through multinational, multiethnic cohorts; improving transparency via open-source preprocessing codes, findable, accessible, interoperable, and reusable-compliant data sharing, and independent validation; and balancing performance and interpretability via explainable DL frameworks to meet clinical ethical standards [66].

We also acknowledge the risk of publication bias, as studies with positive results are more likely to be published, particularly in AI-related research where rapid progress and selective reporting may skew the literature. Additionally, language and geographic biases may exist since only English-language articles were included and most studies originated from a limited number of regions (eg, China, the United States, and Europe). This may limit the generalizability of our findings to underrepresented regions.

Despite ¹⁸F-FDG PET’s higher accuracy, its radiation exposure and cost hinder widespread screening [67]. Conversely, sMRI’s cost-effectiveness and noninvasiveness position it as a first-line screening tool, with PET reserved for confirmatory testing in complex cases—a tiered diagnostic strategy. The 2023 Responsible AI for Social and Ethical Healthcare consensus implementation priorities, including transparent cost-benefit frameworks cross-modal standardization, and dynamic performance monitoring [68].

Although previous reviews have explored the diagnostic accuracy of AI in AD, studies involving meta-analyses remain scarce [69-71]. Conducting such meta-analyses faces significant challenges, particularly due to substantial methodological heterogeneity across studies. This heterogeneity manifests in multiple dimensions, including variations in neuroimaging modalities, disparities in model validation strategies, and differences in algorithm types—all of which influence AD diagnostic performance and complicate the synthesis of evidence.

Borchert et al [70] conducted a comprehensive systematic review of 255 neuroimaging studies utilizing AI for dementia diagnosis and prognosis. Their findings demonstrated that discriminative models, particularly DL approaches, outperformed algorithmic classifiers in distinguishing AD patients from healthy controls. However, they emphasized critical methodological limitations, with conclusions primarily relying on qualitative synthesis rather than quantitative evidence.

In a systematic review and meta-analysis by Sun et al [71], the diagnostic accuracy of DL models based on ¹⁸F-FDG PET for AD was investigated. While the study reported excellent diagnostic performance, notable heterogeneity was observed during meta-analysis, raising concerns about the reliability of the findings. Furthermore, the study focused exclusively on DL, overlooking the widespread application of traditional ML methods in current clinical research for AD diagnostic modeling.

In contrast, our meta-analysis incorporates a broader range of studies, rigorously controls methodological heterogeneity through stringent quality assessment and detailed subgroup analyses, and systematically evaluates the diagnostic accuracy of both ML and DL in AD. By emphasizing methodological rigor and the importance of external validation in AI-assisted neuroimaging for AD diagnosis, this study addresses critical gaps in the existing literature.

Although our subgroup comparisons between ML and DL models provide a useful overview of broad methodological trends, it must be noted that algorithm complexity, training data size, and model optimization procedures vary considerably within each group. The observed performance differences may, therefore, reflect not only model class but also differences in dataset size, feature representation, and implementation quality. Future studies should aim to compare individual algorithms under standardized conditions.

In conclusion, AI can effectively support the diagnosis of AD using sMRI and ¹⁸F-FDG PET imaging. Among these approaches, combining PET imaging with DL techniques yields the highest diagnostic accuracy. These findings suggest that a future direction lies in integrating precision neuroimaging with AI tools. To bring such systems into routine clinical use—helping doctors detect AD earlier, personalize treatment, and improve patient outcomes—future studies should focus on repeated validation with high-quality clinical datasets and the development of standardized implementation protocols.