This systematic review and meta-analysis was conducted in strict accordance with the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 statement (Checklist 1), PRISMA-DTA (PRISMA for Diagnostic Test Accuracy) guidelines, and PRISMA-S (Preferred Reporting Items for Systematic Reviews and Meta-Analyses literature search extension) reporting standards. The study protocol was preregistered in the International Prospective Register of Systematic Reviews (PROSPERO) on May 7, 2024 (registration number: CRD42024545109). All deviations from the preregistered protocol are explicitly listed in Multimedia Appendix 1, with a rationale for each change. Ethical approval and informed consent were not required for this systematic review of published literature [15]. The completed PRISMA 2020, PRISMA-DTA, and PRISMA-S checklists are provided in Checklist 1-4. The following PRISMA-S items were not applicable to this review: (1) item 12 (automated search alerts or updates): no automated alerts were set, as the search was rerun manually at the time of revision; (2) item 13 (gray literature and other resources): the review was restricted to full-text peer-reviewed publications, and no gray literature, trial registries, or unpublished sources were searched; and (3) item 14 (contacting authors for unpublished data): authors were not contacted, as only published diagnostic accuracy data permitting construction of 2×2 contingency tables were eligible for inclusion. These decisions are consistent with the preregistered study protocol (PROSPERO CRD42024545109).

A comprehensive, peer-reviewed literature search was developed in collaboration with a medical librarian, in full adherence to the Cochrane Handbook for Systematic Reviews of Diagnostic Test Accuracy and PRISMA-S guidelines. The search was originally conducted through January 2025 and was fully updated through April 2026 at the time of revision. PubMed, Embase, Cochrane Library, Web of Science, and IEEE Xplore were searched for studies published between January 1, 2014, and April 2026. No geographical restrictions were applied, and only studies published in English were included.

The search strategy combined MeSH terms, Emtree terms, and free-text keywords for three core concepts: (1) SLE and related manifestations, (2) ML and AI, and (3) DTA. Field modifiers were used to restrict terms to the title or abstract fields, where appropriate, to maximize sensitivity and specificity. The full, unedited search strategy for each database is provided in Multimedia Appendix 2.

Additional studies were identified through manual screening of the reference lists of included studies and relevant systematic reviews, to ensure that no eligible studies were missed.

Studies were eligible if they met all of the following criteria. First, regarding study design, eligible studies were full-text, peer-reviewed diagnostic accuracy studies that developed or validated ML or DL models for 1 of the 3 prespecified, clinically homogeneous diagnostic tasks (SLE classification, LN diagnosis, or NPSLE discrimination). Second, regarding the index test, eligible studies used ML or DL models with any type of clinical input data, including histopathology images, radiological images (magnetic resonance imaging [MRI], computed tomography [CT], and ultrasound), spectroscopic data (Raman spectroscopy and Fourier transform infrared spectroscopy [FTIR]), and electronic health record (EHR) data. Third, regarding the reference standard, a clinically accepted independent reference standard was required: for SLE classification, the 1997 ACR, 2012 SLICC, or 2019 EULAR or ACR criteria, or expert consensus by board-certified rheumatologists; for LN diagnosis, renal biopsy (International Society of Nephrology [ISN] or Renal Pathology Society [RPS] classification); and for NPSLE discrimination, the 1999 ACR NPSLE definitions with expert consensus. Fourth, regarding outcome data, studies were required to report sufficient information to construct a 2×2 contingency table (true positive [TP], false positive [FP], false negative [FN], and true negative [TN]) or to provide sensitivity, specificity, and sample size to allow calculation of these values.

Studies were excluded if they met any of the following criteria: nonhuman or animal studies; review articles, editorials, case reports, conference abstracts, letters, or study protocols; studies focused solely on disease prognosis, treatment response prediction, or disease activity score estimation without a primary diagnostic outcome; studies that did not use an independent reference standard or where the reference standard was partially derived from the ML model input features (circular validation); duplicate publications of the same study cohort; or studies with a sample size of fewer than 20 participants.

Two independent reviewers (BW and ZW) performed title and abstract screening in duplicate, followed by full-text screening of potentially eligible studies. Disagreements were resolved by consensus with a third senior reviewer (FG).

Data extraction was performed independently by 3 reviewers (BW, ZW, and YL) using a prepiloted, standardized data extraction form. The form was expanded to include items specific to AI-based diagnostic studies, and all extracted data were cross-checked for accuracy. Discrepancies were resolved by consensus with a fourth reviewer (FG).

The following data were extracted from each included study. Study characteristics included first author, year of publication, study country, study design, study period, clinical setting, sample size, participant demographics, and prespecified inclusion and exclusion criteria. Clinical task details included the explicit definition of the diagnostic task, target population, and clinical decision context. Index test details included the type of ML or DL algorithm, input data modality, model preprocessing steps, training, validation, and testing workflow, and whether the reported model was prespecified or post hoc selected as the best-performing model. Validation strategy details included clear definitions of training, validation, and test sets; whether patient-level splits were used; whether internal or independent external validation was performed; and whether data leakage was assessed and excluded. Reference standard details included the type of reference standard used, definition of positive and negative cases, and whether the reference standard assessment was blinded to the index test results. Diagnostic accuracy outcomes included TP, FP, FN, TN, sensitivity, specificity, area under the curve (AUC), positive predictive value (PPV), negative predictive value (NPV), and 95% CIs, with separate extraction for internal and external validation cohorts. Secondary outcomes included head-to-head comparisons with human clinicians, model calibration, decision-curve analysis (DCA), net clinical benefit, and implementation outcomes. Risk of bias items included all items required for the QUADAS-AI risk of bias assessment.

To avoid double-counting, data dependency, and optimism bias, we implemented the following strict, prespecified rules for including contingency tables in meta-analyses. The following prespecified rules governed contingency table inclusion. For the primary meta-analyses, each independent study cohort contributed exactly one 2×2 contingency table, selected according to the following priority order: first, results from an independent external validation cohort for a prespecified model; second, results from an internal validation cohort for a prespecified model; third, results from the full study cohort for a prespecified model. Post hoc selected best-performing model results were explicitly excluded from all primary analyses to eliminate researcher-driven optimism bias. For subgroup and sensitivity analyses, multiple nonoverlapping contingency tables from the same study were included only if they derived from mutually exclusive patient cohorts with no overlapping participants; all nonindependent data were explicitly labeled and their limitations acknowledged in the paper. Two levels of exploratory analyses were conducted: (1) an exploratory all-task pooled analysis using one table per study (selected using the priority order above) to provide an overall summary, with a clear statement that this analysis has no clinical interpretability; and (2) an exploratory all-table analysis in which all eligible algorithm-level contingency tables from each study were included (124 tables from 29 studies [8,16,17,19-32,34-45]), explicitly treated as exploratory because multiple tables could originate from the same study, potentially introducing within-study correlation.

The risk of bias and applicability concerns of each included study were assessed independently by 2 reviewers (BW and FG) using the QUADAS-AI tool, the validated gold standard for AI-based diagnostic accuracy studies. The QUADAS-AI tool comprises 4 domains: patient selection, index test, reference standard, and flow and timing. Each domain was rated for risk of bias (low, high, or unclear) and applicability concerns (low, high, or unclear), with explicit justifications for each rating. Disagreements were resolved by consensus with a third reviewer (YL).

All statistical analyses were prespecified in the study protocol and performed using R (version 4.4.2; R Core Team) with the mada package for bivariate random-effects meta-analyses. Statistical significance was assessed using a 2-sided α level of .05.

For each of the 3 independent clinical tasks, we performed hierarchical summary receiver operating characteristic (HSROC) meta-analyses to estimate pooled sensitivity, specificity, and AUC. The HKSJ random-effects model was used for all pooled analyses, as this method provides more robust type I error control and more precise effect estimates than the standard DerSimonian-Laird method, particularly in the setting of high between-study heterogeneity and small numbers of included studies.

For all pooled sensitivity and specificity estimates, we reported the pooled point estimate, 95% CI, which quantifies uncertainty around the average effect, and 95% PI, which quantifies the expected range of true effect sizes across different settings for 95% of future similar studies, and provides a clinically relevant estimate of real-world performance variability. The CI and PI serve fundamentally different purposes. The CI reflects the precision of the pooled mean, whereas the PI reflects the distribution of expected effects in new settings, accounting for between-study variance [35].

Between-study heterogeneity was quantified using the I² statistic, with the following thresholds: I²<50%= low heterogeneity, 50%‐75%=moderate heterogeneity,>75%= high heterogeneity,>90%= extreme heterogeneity. The I² statistic has limited utility in practical applications because it cannot quantify the magnitude of true effect variation across populations. Therefore, the 95% PI is used as the primary measure of real-world heterogeneity. For analyses with extreme heterogeneity (I²>90%), the pooled point estimate has limited clinical significance, and the PI should be used to interpret real-world performance.

The certainty of evidence for each analysis was evaluated using the GRADE framework adapted for DTA studies [46,47]. The certainty started at high and was rated down for five domains: (1) risk of bias, downgraded if ≥1/3 of studies had any QUADAS-AI domain rated as high risk; (2) inconsistency, downgraded one level if I²>50% and 2 levels if I²>75% for either sensitivity or specificity; (3) indirectness, downgraded if the study populations, index tests, or reference standards did not directly match the review question; (4) imprecision, downgraded if the number of studies was<5 or the maximum 95% CI width for pooled sensitivity or specificity exceeded 0.20; and (5) publication bias, downgraded if Deeks asymmetry test met the prespecified significance threshold of α=.10. The GRADE assessment was performed for the overall analysis, ML and DL subgroups, each clinical task, and the external validation subgroup.

Prespecified subgroup analyses were performed to explore potential sources of heterogeneity, using the HKSJ model, across the following dimensions: validation strategy (internal validation vs external validation); algorithm type (traditional ML vs DL); input data modality (histopathology vs radiological imaging vs spectroscopic data vs EHR data); sample size (≥100 participants vs <100 participants); and risk of bias (low overall risk vs high or unclear overall risk).

Prespecified sensitivity analyses were performed using the leave-one-out analysis (sequentially removing each study to assess its impact on the pooled estimate), by excluding studies with a high overall risk of bias, and by excluding studies with a sample size<50 participants to assess the robustness of the primary pooled estimates.

Visual inspection of funnel plots and the Deeks funnel plot asymmetry test were used to assess small-study effects. These methods can only assess small-study effects, not publication bias, as publication bias is only one of the many potential causes of small-study effects. Additionally, these analyses have limited statistical power with a small number of included studies and cannot rule out researcher-driven optimism bias from selective reporting of favorable results.

Given that only 2 studies [17,40] reported head-to-head comparisons between ML models and human clinicians, with sparse data, heterogeneous clinical tasks, and varying clinician expertise levels, we performed an exploratory descriptive summary receiver operating characteristic (SROC) analysis only to visualize the comparative diagnostic space; no inferential meta-analysis or formal between-group statistical comparison was attempted, as the data were insufficient to produce reliable pooled estimates.

As this is a systematic review and meta-analysis of published literature, ethical approval and informed consent are not applicable.

A total of 6872 records were retrieved from the electronic database search, with 1159 duplicate records removed, leaving 5713 records for screening. Of these, 5411 records were excluded during initial title and abstract screening, leaving 302 potentially relevant records. A further 195 records were excluded during secondary eligibility screening before full-text retrieval, leaving 107 reports sought for retrieval. All 107 reports were retrieved. Sixty-three reports were excluded during preliminary full-text triage before formal eligibility assessment, leaving 44 reports assessed in detail. Of these, 15 were excluded for the following reasons: not a diagnostic accuracy study (n=12), incomplete data for construction of a 2×2 table (n=2), and research topic mismatch (n=1). The remaining 29 eligible studies comprised 25 studies included in the previous version of the review [8,16,17,19-32,34-41] and 4 newly included studies [42-45], yielding a total of 29 studies in the updated review. The detailed study selection process is shown in Figure 1.

A total of 29 studies met all criteria for the quantitative meta-analysis [8,16,17,19-32,34-45]. Aliyev et al [48] and de Araújo et al [33] were excluded from all analyses. The 29 studies were distributed across the 3 prespecified clinical tasks as follows: 17 studies for SLE classification [8,21,23,24,27,29-31,34-37,40-44], 5 studies for LN diagnosis [19,20,22,26,32], and 7 studies for NPSLE discrimination [16,17,25,28,38,39,45], with no overlapping patient cohorts across tasks. In the all-table exploratory analysis, 124 tables from 29 studies were included [8,16,17,19-32,34-45]. The exploratory receiver operating characteristic (ROC) results stratified by task type and disease type are shown in Figures 2 and 3, respectively. The pooled overall ROC analysis across all included studies is presented in Figure S1 in Multimedia Appendix 3. The forest plot for the all-table exploratory analysis is presented in Figure S3 in Multimedia Appendix 3.

The baseline characteristics of the 29 included studies [8,16,17,19-32,34-45] are summarized in Tables S1-S3 in Multimedia Appendix 3. The studies were published between 2018 and 2026, with sample sizes ranging from 26 to 6476 participants. All included studies were retrospective in design. Of the 29 studies [8,16,17,19-32,34-45], 9 (31%) [21,23,24,28,32,38,40,42,45] performed independent external validation using out-of-sample, multicenter, or temporally separated cohorts; the remaining 20 (69%) [8,16,17,19,20,22,25-27,29-31,34-37,39,41,43,44] used only internal validation (random split-sample or k-fold cross-validation within a single dataset). Study design and basic demographic characteristics are summarized in Table S3 in Multimedia Appendix 3; the methods of model training and validation are summarized in Table S1 in Multimedia Appendix 3; indicators, algorithms, and data sources are summarized in Table S2 in Multimedia Appendix 3; terminology mapping across included studies is provided in Table S4 in Multimedia Appendix 3; and the implementation and reporting checklist is provided in Table S5 in Multimedia Appendix 3.

The included studies covered 3 primary clinical tasks, including SLE classification or diagnosis (17 studies) [8,21,23,24,27,29-31,34-37,40-45], LN diagnosis and classification (5 studies) [19,20,22,26,32], and NPSLE discrimination (7 studies) [16,17,25,28,38,39,45]. Input data modalities included histopathology images (9 studies, comprising 7 independent patient cohorts) [8,20-24,29,32,37], MRI (8 studies) [16,17,25,28,36,38,39,45], Raman spectroscopy (3 studies) [34,35,41], clinical images (3 studies) [27,30,40], retinal fundus imaging (1 study) [42], nailfold videocapillaroscopy (1 study) [44], optical coherence tomography (OCT; 1 study) [31], ultrasound (1 study) [26], finger optical diffusion imaging (FODI; 1 study) [19], and EHR and laboratory data (1 study) [43]. For subgroup meta-analysis by modality, retinal fundus imaging and nailfold videocapillaroscopy were grouped with clinical images (5 studies total) [27,30,40,42,44], and only modality subgroups represented by at least 3 studies were analyzed separately. Only 2 studies (6.9%) [40,42] performed head-to-head comparisons between ML models and board-certified rheumatologists or dermatologists using the same held-out test dataset. None of the included studies reported model calibration, DCA, or net clinical benefit.

The results of the QUADAS-AI risk of bias assessment are presented in Figures 4 and 5. Overall, 22 out of 29 studies (75.9%) [8,17,19-22,24-28,30,34-39,41-43,45] were judged to have high or unclear overall risk of bias.

In the domain of patient selection, 18 (62.1%) [8,17,19,21,25-28,30,34-36,38,39,41-43,45] studies had high or unclear risk of bias, primarily due to nonconsecutive patient recruitment, case-control design that did not reflect the clinical target population, or inappropriate exclusion criteria. For the index test, 27 (93.1%) [8,16,17,20-32,34,35,37-45] studies had low risk of bias, while 1 (3.4%) [36] study had unclear risk of bias and 1 (3.4%) study [19] had high risk of bias. For reference standards, 24 (82.8%) [8,16,17,20-24,27-32,34,35,37,39-45] studies had low risk of bias, 2 (6.9%) [36,38] studies had unclear risk of bias, and 3 (10.3%) [19,25,26] studies had high risk of bias, primarily due to lack of blinding of the reference standard assessment to the index test results or inconsistent application of the reference standard. Regarding flow and timing, 19 (65.5%) [8,17,19,20,22,24,27,28,30,34-39,41-43,45] studies had high or unclear risk of bias, primarily due to lack of reporting of the time interval between the index test and reference standard, or exclusion of participants from the final analysis without justification.

For applicability concerns, 4 (13.8%) [36,38,42,44] studies had unclear concerns related to patient selection. For the index test, 2 (6.9%) [19,36] studies had unclear concerns. For the reference standard, 3 (10.3%) [35,36,42] studies had unclear concerns, and 4 (13.8%) [17,20,24,25] studies had high concerns.

The HKSJ random-effects model was used for all primary analyses, with one independent contingency table per study, prioritizing external validation and prespecified model results. In the primary analysis of all 29 studies [8,16,17,19-32,34-45], the pooled sensitivity was 0.91 (95% CI 0.86‐0.94, 95% PI 0.56‐0.99) and the pooled specificity was 0.94 (95% CI 0.91‐0.96, 95% PI 0.69‐0.99), with low between-study heterogeneity (I²=23.9% for sensitivity, I²=22.9% for specificity). Deeks funnel plot asymmetry test showed no significant small-study effects (P=.19). The Cochrane-style forest plot for the primary analysis is shown in Figure 6. The forest plot for the primary task-stratified analysis is also presented in Figure S2 in Multimedia Appendix 3.

A total of 17 studies (one independent contingency table per study) were included in the primary analysis for SLE classification (Task 1) [8,21,23,24,27,29-31,34-37,40-44]. The pooled results showed a sensitivity of 0.90 (95% CI 0.84‐0.94, 95% PI 0.53‐0.99) and specificity of 0.94 (95% CI 0.92‐0.96, 95% PI 0.85‐0.98). Low between-study heterogeneity (I²=24.7% for sensitivity, I²=6.7% for specificity) was observed. The CI, reflecting precision of the average effect, was relatively narrow, whereas the PI, reflecting the expected distribution of performance in new settings, was considerably wider. This distinction is critical: the narrow CI indicates that the average performance is precisely estimated, while the wide PI (sensitivity 0.53‐0.99) indicates that a new study conducted in a different setting could yield substantially different results depending on population characteristics, imaging modality, and reference standard [35]. According to the GRADE assessment, the certainty of evidence was high for SLE classification (Table 1).

The GRADE framework was used to assess the certainty of evidence for DTA. Certainty starts at high and is rated down for risk of bias when at least one-third of the included studies have at least one QUADAS-AI domain rated as high risk, inconsistency (I²>50% one level and >75% 2 levels), indirectness, imprecision (k<5 or 95% CI width>0.20 for sensitivity or specificity), and publication bias (Deeks test significance threshold α=.10, where assessed). I² represents between-study heterogeneity, and CI denotes confidence interval.

Five studies (one independent contingency table per study) were included in the primary analysis for LN diagnosis (Task 2) [19,20,22,26,32]. The pooled results showed a sensitivity of 0.93 (95% CI 0.86‐0.97, 95% PI 0.68‐0.99) and specificity of 0.95 (95% CI 0.76‐0.99, 95% PI 0.19‐1.00). Low-to-moderate between-study heterogeneity (I²=18.4% for sensitivity, I²=56.4% for specificity) was observed. The wide PI for specificity (0.19‐1.00), driven by moderate heterogeneity (I²=56.4%), indicates variability in reference standard definitions and patient population composition across LN studies. Caution should be exercised when generalizing these estimates to new clinical settings. According to the GRADE assessment, the certainty of evidence was low for LN diagnosis, downgraded for inconsistency (I²=56.4% for specificity) and imprecision based on the 5 included studies [19,20,22,26,32] and a maximum CI width of 0.23 (Table 1). This low certainty of evidence indicates that the true diagnostic performance may be substantially different from the pooled estimate.

Seven studies (one independent contingency table per study) were included in the primary analysis for NPSLE discrimination (Task 3) [16,17,25,28,38,39,45]. The pooled results showed a sensitivity of 0.88 (95% CI 0.76‐0.95, 95% PI 0.54‐0.98) and specificity of 0.89 (95% CI 0.76‐0.95, 95% PI 0.50‐0.99). Between-study heterogeneity was low (I²=18.0% for sensitivity, I²=21.7% for specificity). The low heterogeneity makes the pooled point estimate more clinically interpretable. However, the wide PIs (sensitivity 0.54‐0.98, specificity 0.50‐0.99) indicate that in a new clinical setting, the expected performance could vary substantially, reflecting differences in imaging modality, patient selection criteria, and NPSLE definition across studies [49]. According to the GRADE assessment, the certainty of evidence was high for NPSLE discrimination (Table 1). The forest plots for each clinical task are presented in Figure S4 in Multimedia Appendix 3.

An exploratory pooled analysis of all 29 studies (one independent table per study) [8,16,17,19-32,34-45] yielded a pooled sensitivity of 0.91 (95% CI 0.86‐0.94, 95% PI 0.56‐0.99), specificity of 0.94 (95% CI 0.91‐0.96, 95% PI 0.69‐0.99), and AUC of 0.969 (SROC), with low between-study heterogeneity (I²=23.9% for sensitivity, I²=22.9% for specificity; Deeks P=.19). This analysis is presented for methodological exploration only. Since these pooled point estimates combined heterogeneous and incomparable clinical tasks, they lacked clinical or statistical significance and should not be used to infer the overall diagnostic performance of ML models for SLE.

The GRADE assessment results are summarized in Table 1. The overall certainty of evidence was rated as high for most analyses, including the primary analysis of all 29 studies [8,16,17,19-32,34-45], the ML and DL subgroups, SLE classification, NPSLE discrimination, and external validation (Table 2). The certainty of evidence for LN diagnosis was rated as low due to inconsistency (I²=56.4% for specificity) and imprecision (k=5 studies [19,20,22,26,32], maximum CI width=0.23). These results indicate that while the pooled estimates for most analyses are reliable, the evidence for LN diagnosis should be interpreted with caution, and additional studies are needed to increase confidence in the pooled estimates for this task.

Our principal finding is that ML models show promising in-sample diagnostic accuracy across all 3 prespecified clinical tasks. In the primary task-stratified analyses, the pooled sensitivity and specificity were 0.90 and 0.94, respectively, for SLE classification (n=17) [8,21,23,24,27,29-31,34-37,40-44]; 0.93 and 0.95, respectively, for LN diagnosis (n=5) [19,20,22,26,32]; and 0.88 and 0.89, respectively, for NPSLE discrimination (n=7) [16,17,25,28,38,39,45], and SROC AUC values of 0.940 (SLE), 0.938 (LN), and 0.877 (NPSLE) in the all-table exploratory analyses. However, these promising results must be interpreted with caution for several reasons. First, all included studies were retrospective, and only 9 [21,23,24,28,32,38,40,42,45] of 29 (31%) [8,16,17,19-32,34-45] studies performed independent external validation. Second, while between-study heterogeneity was substantially lower in the updated analysis than the previous version (I²=23.9% overall for sensitivity, compared with I²=97.5% previously), the PIs remained wide for most analyses, reflecting significant variations in model performance across different clinical populations, imaging modalities, and institutional contexts [49,50]. Third, reference standards were inconsistent across studies, with some relying on retrospective clinical labels rather than prospectively applied standardized classification criteria [51]. Fourth, no included study assessed model calibration, DCA, or net clinical benefit, suggesting that high AUC values do not prove that the model is ready for clinical application [52]. Fifth, the GRADE assessment confirmed high certainty of evidence for most analyses but low certainty for LN diagnosis due to inconsistency and imprecision. Hence, additional studies are needed before pooled LN estimates can be confidently applied in clinical practice [46,47]. Our analysis also confirms that internal validation systematically overestimates ML model performance relative to external validation, which is commonly observed across diagnostic ML research and is not unique to SLE [53,54].

Our findings build on and address the fundamental limitations of prior systematic reviews in this field, with 4 key contributions to the literature. First, we addressed the core conceptual flaw of prior reviews by performing fully task-stratified meta-analyses, rather than pooling heterogeneous clinical tasks into a single analysis [55]. This ensures the clinical interpretability and methodological validity of our pooled estimates and aligns with the core assumptions of DTA meta-analysis. Prior reviews have combined SLE classification, LN activity grading, NPSLE discrimination, and disease activity estimation into a single pooled analysis, yielding results that lack practical value in both statistical and clinical terms. Our task-stratified approach resolves this critical issue [56]. Furthermore, this task-stratified approach revealed significant differences in the certainty of evidence across tasks: while SLE classification and NPSLE discrimination achieved high GRADE certainty, LN diagnosis was rated as low certainty, a distinction that would have been obscured by pooling all tasks together.

Second, we use state-of-the-art statistical methods for DTA meta-analysis, including the HKSJ random-effects model and 95% PIs, which can account for extreme between-study heterogeneity [49]. Unlike prior reviews that overinterpreted pooled AUC values in the setting of I²>95%, we explicitly acknowledged the limitations of pooled point estimates with extreme heterogeneity and used PIs to quantify the real-world variability in model performance [57]. For instance, the primary analysis for SLE classification showed a relatively narrow CI (sensitivity 0.84‐0.94) but a wide PI (sensitivity 0.53‐0.99). It indicates that while the average performance is precisely estimated, a new study in a different population could yield markedly different results [35]. This avoids the statistical misinterpretations in previous reviews that led to inaccurate conclusions [58].

Third, we implemented strict rules for including contingency tables to eliminate data dependency, double counting, and optimism bias. Prior reviews extracted multiple nonindependent contingency tables from the same study (from multiple models, thresholds, or cross-validation splits), treating them as independent observations and leading to artificially narrow CIs and inflated precision [59]. In our primary analyses, we adhered to the principle of using only one independent table per study and excluded post hoc best-performing model results, thereby resolving this methodological flaw [60]. Fourth, we systematically distinguished between internal and external validation results and quantified the overestimation of performance from internal validation [61,62]. Prior reviews have confounded internal and external validation results, leading to overestimations of real-world generalizability [63]. Internal validation methods, such as k-fold cross-validation and random split-sample validation, estimate model performance within the same dataset used for training, and are therefore susceptible to optimistic bias from dataset-specific patterns, overfitting to demographic or institutional characteristics, and data leakage. In contrast, independent external validation tests the model on entirely new data from different institutions, time periods, or geographic settings, providing a more realistic estimate of real-world performance [54,62]. In the updated analysis, 9 [21,23,24,28,32,38,40,42,45] of 29 (31%) [8,16,17,19-32,34-45] studies performed external validation, and the PI for externally validated studies (sensitivity 0.32‐0.99, specificity 0.53‐0.99) underscores the high variability of ML model performance across clinical contexts. We prioritized external validation results in all primary analyses [64].

The included studies have several major methodological limitations that severely undermine the validity and clinical applicability of their findings. First, all included studies were retrospective in design, which introduces a high risk of bias, including selection bias, data leakage, and overfitting. Retrospective ML model development typically relies on convenience samples that do not reflect the target clinical population, and models may learn spurious correlations from the data that do not generalize to real-world settings [65]. No prospective studies of ML for SLE diagnosis were identified in this review. Second, the vast majority of studies used only internal validation, with only 31% (9/29) performing independent external validation. Internal validation is well known to systematically overestimate diagnostic accuracy, particularly in ML studies with flexible modeling pipelines and limited sample sizes [53]. Our subgroup analysis confirmed this, showing significantly lower performance in externally validated studies [56]. Without independent, multicenter external validation, the real-world generalizability of these models remains unproven [66].

Third, despite the low overall between-study heterogeneity (I²=23.9%), the PIs remained wide for most analyses, indicating that the expected performance of ML models in any single new clinical setting could vary substantially. This is partially explained by differences in data modality, validation strategy, and sample size [50]. The remaining heterogeneity is likely due to differences in study population, reference standard definition, model development workflow, and preprocessing steps, which limit the generalizability of pooled estimates [67]. The wide 95% PIs for most analyses confirm that model performance is highly variable across different clinical settings and populations [54]. Fourth, there was significant inconsistency in the reference standards used across studies. Some studies used retrospective clinical labels rather than standardized classification criteria, and a small number of studies used reference standards that were partially informed by the same data used to train the ML model, thereby introducing the risk of circular validation and bias in the reference standard [51]. This inconsistency further limits the comparability of results across studies [55].

Fifth, researcher-driven optimism bias is a pervasive risk across all included studies. Many studies reported only results of the best-performing model, without prespecifying the primary model or accounting for multiple comparisons [68]. This selective reporting leads to an overestimation of model performance and cannot be ruled out even in the absence of statistically significant small-study effects [69]. Finally, none of the included studies assessed the clinical utility of their models. High AUC values alone do not prove that the model can improve patient outcomes in clinical practice; a model with high discriminative accuracy may still cause net harm if it is poorly calibrated, its decision threshold is inappropriate for the target clinical population, or it leads to overdiagnosis, unnecessary invasive testing, or inappropriate immunosuppressive treatment. Model calibration refers to the agreement between the model’s predicted probabilities and the actual observed outcome frequencies across the probability range, and is typically assessed using calibration plots, the Hosmer-Lemeshow test, or the expected calibration error (ECE). DCA is the recommended framework for evaluating whether a diagnostic model provides net clinical benefit over default strategies (treat-all or treat-none) across a range of clinically plausible decision thresholds [52]. Without such formal assessments and prospective evaluation of the model’s impact on diagnostic workflow, patient management decisions, and clinical outcomes, it is impossible to determine whether these ML models would provide meaningful benefit to patients with SLE in real-world clinical practice.

This review has several limitations that should be acknowledged. First, we only included studies published in English, which may introduce language bias [70]. Second, we excluded conference abstracts, which may lead to publication bias, as negative or nonsignificant results are less likely to be published in full-text peer-reviewed journals. Third, the number of included studies for some subgroup analyses was small, limiting statistical power, and these analyses are therefore presented as exploratory only. Fourth, we were unable to perform meta-analysis of individual patient data, which would have allowed for more robust adjustment for confounding factors and more detailed subgroup analyses [71]. Finally, we were unable to assess the risk of data leakage in the included studies, as this is often not reported in detail, which may lead to an overestimation of model performance in the original studies [72,73]. Additionally, the GRADE framework, while widely used for assessing certainty of evidence, has limitations when applied to DTA studies. It was originally developed for intervention studies and may not fully capture all sources of uncertainty in diagnostic accuracy meta-analyses [46].

The findings of this review have critical implications for future research and clinical practice. For future research, we make the following evidence-based recommendations. First, future ML studies for SLE diagnosis must be prospectively designed, with preregistration of the study protocol, model development plan, and statistical analysis plan, to reduce the risk of bias and selective reporting [65,68]. Second, all ML models must undergo independent, multicenter external validation in cohorts that reflect the target clinical population, to confirm real-world generalizability [54,62,66]. Third, future studies must use clearly defined, clinically homogeneous diagnostic tasks and consistent reference standards to reduce heterogeneity and enable meaningful comparison between models [55,69]. Fourth, all future studies must assess clinical utility, including model calibration, DCA to quantify net clinical benefit, and evaluation of the model’s impact on diagnostic workflow and patient outcomes [52]. Fifth, future studies should perform prespecified, head-to-head comparisons between ML models and board-certified rheumatologists, using standardized test datasets and clearly defined clinician expertise levels, to determine the incremental value of ML-assisted diagnosis over standard clinical care.

For clinical practice, our review confirms that ML models for SLE diagnosis are not yet ready for routine clinical application [74]. The current evidence is of variable quality, with GRADE certainty ranging from high (for most analyses) to low (for LN diagnosis), due to exclusively retrospective designs, lack of independent external validation, wide PIs, and absence of clinical utility assessment [75]. There is currently no evidence that these models improve patient outcomes in real-world clinical settings [76]. At this stage, ML should only be used as an auxiliary tool to support expert clinical judgment, in the context of prospective research studies, until robust, externally validated, clinically beneficial models are developed [77,78].

This is the first methodologically rigorous, task-stratified systematic review and meta-analysis of ML models for SLE diagnosis, with formal GRADE assessment of certainty of evidence, addressing the core conceptual and statistical flaws of prior syntheses. ML models show promising in-sample diagnostic accuracy for 3 distinct SLE-related clinical tasks, but the current evidence is of variable certainty (high for most analyses, low for LN diagnosis), limited by pervasive methodological weaknesses, including exclusively retrospective designs, lack of independent external validation, wide PIs despite low I², and absence of clinical utility assessment. The distinction between the narrow CIs (reflecting precision of the average effect) and the wide PIs (reflecting expected variability across new settings) is critical for clinical interpretation: the pooled estimates should not be taken as guaranteed performance in any individual new setting [35]. Future research must prioritize prospectively registered, multicenter, externally validated studies with standardized clinical tasks, harmonized reference standards, and formal assessment of clinical utility, to support the safe and effective translation of ML tools into clinical care for SLE.