We conducted and reported the literature search in accordance with the PRISMA-S (Preferred Reporting Items for Systematic Reviews and Meta-Analyses Literature Search Extension) statement [20]. A comprehensive systematic search was performed across 8 electronic databases: PubMed/MEDLINE, PsycINFO, Web of Science, EMBASE, Scopus, ProQuest Dissertations and Theses, Cochrane Library, and ClinicalTrials.gov (for gray literature). The search covered January 1, 2000, to May 22, 2026, with no language restrictions.

We used a combination of controlled vocabulary (eg, MeSH) and free-text terms, optimized for each database platform. The full, exact search strategy for each database is provided in Multimedia Appendix 1.

Database searches were supplemented by citation searching (snowballing), that is, screening the reference lists of all included studies and relevant systematic reviews. No additional searches of conference proceedings, clinical trial registries beyond ClinicalTrials.gov, or expert contacts were performed.

All retrieved records were merged and deduplicated using reference management software prior to screening.

Two reviewers (HX and BW) independently screened all retrieved records at the title and abstract stage, followed by full-text screening for potentially eligible studies. Any discrepancies regarding eligibility were resolved through discussion or by consulting a third reviewer (CW) until consensus was reached. The flow of study selection was documented and reported in accordance with PRISMA 2020 guidelines.

Data extraction and quality assessment of the included studies were independently conducted by 2 reviewers (ZH and BW). Any disagreements were resolved through discussion and consultation with a third reviewer (ZQ). The study selection process proceeded as follows: first, titles were screened to exclude irrelevant studies. Subsequently, abstracts and full texts were further reviewed, and studies were evaluated against the predefined inclusion and exclusion criteria to determine eligibility. When critical information was missing, the corresponding authors of the original studies were contacted via email or telephone.

The participant samples across all included studies were mutually independent, and no duplicate counting of participants occurred in the NMA. For multiarm trials, only data from arms that fulfilled the inclusion criteria were included in the analyses.

The following data were extracted: (1) first author and year of publication; (2) study design; (3) age of participants; (4) sample size; (5) IQ scores of participants (assessed using the Wechsler Intelligence Scale for Children, Fourth Edition [WISC-IV]); (6) sex ratio (male/female); (7) interventions in the experimental and control groups; (8) intervention duration; and (9) outcome measures. All extracted data were entered into a Microsoft Excel spreadsheet.

We assessed the risk of bias for all eligible studies. Two reviewers (ZH and HX) independently evaluated each included RCT using the Revised Cochrane Risk of Bias (RoB 2) tool [23], and disagreements were resolved through discussion with a third reviewer (CW). RoB 2 assesses bias across 5 domains: the randomization process, deviations from intended interventions, missing outcome data, measurement of the outcome, and selection of the reported result. Each domain is judged as low risk, some concerns, or high risk according to the official RoB 2 guidance. Given that parents served as outcome assessors in all included trials and could not be blinded to treatment allocation due to the nature of the interventions, we systematically assessed this source of bias within domain 4 (measurement of the outcome) of the RoB 2 tool. The overall risk of bias was determined as follows: low risk if all domains were low risk, some concerns if at least one domain raised some concerns and no domain was high risk, and high risk if at least 1 domain was rated high risk.

All outcomes included in this study were continuous variables. The mean difference (MD) was selected as the primary effect measure. For conventional pairwise meta-analyses, the pooled effects were presented with 95% CI; for the Bayesian NMA, the estimates were quantified using posterior medians with 95% credible intervals (CrI). The MD was preferred over the standardized mean difference because all included studies used identical, widely validated assessment instruments for each outcome domain, allowing for direct comparison of effect sizes in their original clinical units and substantially enhancing the interpretability of findings for clinical practice. Core ADHD symptoms were assessed using the ADHD-RS and the SNAP-IV, including its PI and PHI subscales, while executive functions were assessed using the global executive composite score of the BRIEF parent version. For all scales, lower scores indicated less severe symptoms and better functional outcomes. For pairwise meta-analyses, statistical significance was determined by whether the 95% CI for the MD crossed zero; for Bayesian NMA, the analogous criterion was whether the 95% CrI crossed zero.

Data were synthesized using a Bayesian NMA with random-effects models, implemented via the R software (version 4.2.3; R Foundation for Statistical Computing) packages gemtc and JAGS (version 4.3.0) [24]. For conventional pairwise meta-analyses, the restricted maximum likelihood (REML) method was used to estimate the between-study heterogeneity variance, and 95% CI values were calculated using the Hartung-Knapp-Sidik-Jonkman (HKSJ) method [25,26]. Compared with the conventional DerSimonian-Laird (DL) method, this approach provides more robust statistical inference and better controls the type I error rate, which is particularly advantageous in scenarios with a limited number of studies and substantial heterogeneity [26]. All data conversions were performed in accordance with the formulas recommended in the Cochrane Handbook for Systematic Reviews of Interventions (version 6.2) [27]: SD=(N)∗(upperlimit−lowerlimit)3.92 and SD=N∗SE. Specifically, CI and SE were transformed into SD. Only after all data conversions were completed were the data included in subsequent analyses. Model parameters were specified using vague prior distributions: a normal distribution with a mean of 0 and variance of 10⁴ was adopted for effect sizes (MD), while a uniform distribution with a scale parameter of 2.5 was used for the between-study heterogeneity variance. All models were implemented using 4 Markov chains, each run for 500,000 iterations, with the first 20,000 iterations discarded as the burn-in period. Thinning was applied at an interval of every 10 iterations [28]. Posterior estimates of treatment effects were summarized as posterior medians with 95% CrI. In contrast to frequentist CI, CrI provide a probabilistic interpretation of the parameter uncertainty, indicating the range within which the true effect size lies with 95% posterior probability [29]. Convergence was comprehensively assessed using the potential scale reduction factor (PSRF<1.05), alongside visual inspection of trace plots and density plots [30].

Given the potential heterogeneity among the included studies, a random-effects model was used for the NMA of both direct and indirect comparisons among interventions. This model offers a distinct advantage in that it provides relatively conservative estimates while effectively accounting for part of the heterogeneity across studies, thereby yielding more robust evidence for the conclusions [31]. Model parameters were specified using vague prior distributions to obtain posterior probability distributions for the relative effects of each treatment, thereby quantifying the uncertainty surrounding parameter estimates.

Heterogeneity was quantified using the I² statistic and between-study variance (τ²). However, because I² does not reflect the actual dispersion of true treatment effects across populations, we computed 95% prediction intervals (PI) based on the network estimates to quantify the real-world implications of heterogeneity [32]. In contrast to CI, which quantify the precision of the pooled average estimate, PI estimate the range of true effects that could be expected in a future individual study or clinical setting [32]. For NMA, PI were constructed using the t-distribution approximation method recommended by Noma et al [33].

To comprehensively explore potential sources of heterogeneity, a 3-stage strategy was implemented. First, the clinical magnitude of heterogeneity was assessed primarily via the width and coverage of PI. PI were consistently wider than their corresponding CI, indicating that between-study heterogeneity introduces additional uncertainty when extrapolating pooled effect estimates to future independent studies. The I² statistic was reported solely as a descriptive supplementary metric. Second, subgroup analyses were conducted for categorical variables (eg, age group and sex ratio), and meta-regression analyses were performed for continuous variables (eg, intervention duration and year of publication). Third, a leave-one-out sensitivity analysis was conducted to identify individual studies exerting a dominant influence on the pooled effect sizes and to evaluate the robustness of the findings.

Network relationships among the included interventions were illustrated using a network graph. In this graph, nodes represent various interventions, with the size of each node reflecting the sample size associated with that specific intervention. Lines connecting the nodes indicate direct comparisons between pairs of interventions, and the thickness of these lines corresponds to the number of studies supporting each comparison; thicker lines represent a greater number of relevant studies [34]. A consistency model was applied when no closed loops were formed among the studies. In the presence of closed loops within the network graph, both global and local inconsistency tests were conducted [35]. Global inconsistency was evaluated by comparing the deviance information criterion (DIC) values between the consistency model and an inconsistency model (unrelated mean effects model). A smaller DIC value indicated a better model fit, and a difference of 5 or more was considered indicative of meaningful inconsistency. Local inconsistency was assessed using the node-splitting method for each closed loop in the network. For node-splitting results, a P value greater than .05 was considered indicative of no significant inconsistency between direct and indirect effect estimates. The consistency model was used as the primary analysis model unless significant inconsistency was identified. In the network model of this study, conventional interventions were categorized into 2 distinct nodes based on their nature: conventional nonpharmacological therapy and conventional pharmacotherapy. This separation was based on the following considerations: (1) the 2 types of interventions have fundamentally different mechanisms of action and effect sizes; (2) previous NMAs have demonstrated significant heterogeneity in their efficacy on core ADHD symptoms [36]; and (3) transitivity tests confirmed that the 2 intervention types were comparable in terms of study design and patient characteristics, satisfying the underlying assumptions of NMA.

Additionally, treatment effects were ranked by generating bar charts of SUCRA values. A larger area under the curve indicated a higher ranking of the intervention’s treatment effect [37]. Furthermore, forest plots were generated to present the results of meta-analyses.

Small-study effects were assessed using funnel plots and Egger linear regression test for all outcome domains with 10 or more included studies, as recommended by the Cochrane Handbook for Systematic Reviews of Interventions [27]. Funnel plots and Egger test were selected due to their acceptable statistical power for detecting small-study effects in meta-analyses with a moderate number of studies [38,39]. A P value greater than .05 was considered indicative of no significant small-study effects. For outcome domains with fewer than 10 included studies, quantitative assessment of small-study effects was not performed due to limited statistical power. Potential biases are discussed qualitatively in the Limitations section.

Two reviewers (ZH and CW) independently assessed the certainty of evidence for each pairwise comparison, with any disagreements resolved through discussion with a third reviewer (ZQ). The certainty of evidence was evaluated using the GRADE (Grading of Recommendations Assessment, Development and Evaluation) approach adapted for NMA [40]. Evidence certainty was rated across 5 domains (risk of bias, inconsistency, indirectness, imprecision, and publication bias) as high, moderate, low, or very low in accordance with standard GRADE guidance [41].

This systematic review and NMA were conducted according to the protocol prospectively registered in the International Prospective Register of Systematic Reviews (PROSPERO) under registration number CRD420261304236.

All deviations from the registered protocol are reported below. None materially altered the core research question, study design, or primary conclusions.

No other deviations from the registered protocol occurred.

The initial database search yielded 6209 records. After removing 2258 duplicate records, the remaining 3951 records were screened based on titles and abstracts, resulting in the exclusion of 3739 articles that did not meet the inclusion criteria. An additional 10 articles were excluded because full texts could not be retrieved, leaving 202 articles for full-text assessment. During full-text evaluation, 42 articles were excluded due to ineligible study design, 34 articles were excluded due to ineligible study population age, 31 articles were excluded due to ineligible interventions, 48 articles were excluded due to outcome measures not meeting the inclusion criteria, and 20 articles were excluded due to unavailable data. Furthermore, an additional 5 articles were identified through snowballing and citation searching and included. Ultimately, a total of 32 articles were included in this NMA. The detailed screening process is presented in Figure 1.

Table 2 shows that a total of 32 studies comprising 2819 patients were included in this NMA, with 1431 patients in the experimental groups and 1388 in the control groups. Regarding study design, 9 studies were 3-arm trials [44-52], and 23 were 2-arm trials [10,12-14,53-71]. For the 3-arm trials, only arms meeting the inclusion criteria were included in the analysis; arms that did not meet the inclusion criteria were excluded from statistical synthesis. With respect to the classification of experimental interventions, 17 studies used single-task DTx (n=559) [44-49,53-63], 4 studies used cognitive-motor dual-task DTx (n=149) [50,51,64,66], 4 studies used AI-integrated single-task DTx (n=69) [13,14,65,67], and 7 studies used AI-integrated cognitive-motor dual-task DTx (n=610) [10,12,52,68-71]. All key data required for the analyses (including sample sizes, effect estimates, and measures of variance) were fully extractable from the published articles or the available supplementary materials. Consequently, the prespecified contact procedure for missing information was not triggered, and no corresponding authors were contacted for additional data. The specific details are shown in Table 2.

The risk of bias of the included studies was assessed using the RoB 2 tool. The overall risk of bias assessment revealed that 37.5% of the studies were rated as “low risk,” 21.9% as having “some concerns,” and 40.6% as “high risk,” largely due to inadequate reporting of randomization methods and blinding procedures. A major contributing factor is that, in many studies, parents (the outcome assessors) were unable to be blinded to group allocation. Although this limitation was systematically assessed in domain 4 of RoB 2, we did not exclude these studies from the primary analysis; instead, their potential influence was evaluated post hoc through sensitivity analyses. Detailed information is presented in Figures 2 and 3 and Multimedia Appendix 2.

For the SNAP-IV (both PI and PHI subscales) and the BRIEF, although the pooled mean effects were statistically significant (with 95% CI excluding the null), the corresponding 95% PI all crossed zero. This indicates that the observed treatment effects for these outcomes may exhibit considerable heterogeneity when generalized to future pediatric populations with different characteristics. In contrast, the 95% PI for the ADHD-RS did not cross zero, confirming that the findings for this outcome are characterized by robust external validity and low between-study heterogeneity (Figure 5).

Descriptively, I² values were below 50% for the ADHD-RS and exceeded 50% for the BRIEF, SNAP-IV-PI, and SNAP-IV-PHI. These values are presented for descriptive purposes only and were not used to classify the severity of heterogeneity (see Figures S7A-S7D in Multimedia Appendix 3). Subgroup analyses, sensitivity analyses, and meta-regression were subsequently performed to explore potential sources of between-study variation.

To explore potential sources of heterogeneity, meta-regression analyses were conducted, with year of publication, intervention duration, and mean participant age as covariates. The results showed that none of these 3 variables significantly moderated the pooled effect sizes for the BRIEF or the SNAP-IV (both PI and PHI subscales; see Figures S8A-S10C in Multimedia Appendix 3).

Given that heterogeneity tests revealed significant heterogeneity across outcome measures on the SNAP-IV (both PI and PHI subscales) and the BRIEF, further subgroup analyses were conducted to explore potential sources of heterogeneity in these outcomes. Subgroup analyses were performed based on intervention duration, mean participant age, and sex ratio.

Subgroup analyses stratified by intervention duration revealed substantially reduced heterogeneity within specific subgroups. Specifically, for the SNAP-IV-PI subscale, no significant heterogeneity was observed in the 7-week subgroup (I²=0%; MD −1.11, 95% CI −1.23 to −0.98). However, aside from the 7-week subgroup, heterogeneity remained substantial (I²>50%) in other intervention duration subgroups (eg, 4-week and 5-week), suggesting that the explanatory role of intervention duration for heterogeneity may be confined to specific duration intervals. For the SNAP-IV-PHI subscale, the 3-month subgroup also demonstrated low heterogeneity (I²=0%; MD −0.97, 95% CI −1.30 to −0.64). For the BRIEF, heterogeneity was substantially reduced in the 6-week subgroup (I²=0%; MD −5.23, 95% CI −9.46 to −1.00). Moreover, the overall results of these subgroup analyses were statistically significant (all P<.001; Figures S11A-S11C in Multimedia Appendix 3). These findings suggest that intervention duration represents a potential source of heterogeneity, influencing scores on the SNAP-IV (both PI and PHI subscales) and the BRIEF (see Figures S11A-S11C in Multimedia Appendix 3).

Subgroup analyses based on mean participant age categorized participants into 3 subgroups: preschool children (4 years≤age<6 years), school-aged children (6 years≤age<12 years), and adolescents (12 years≤age≤17 years). The results demonstrated substantially reduced heterogeneity within specific subgroups. Specifically, for the SNAP-IV-PI subscale, no significant heterogeneity was observed in the adolescent subgroup (I²=0%; MD −0.83, 95% CI −1.11 to −0.54). For the BRIEF, heterogeneity was substantially reduced in the adolescent subgroup (I²=0%; MD −2.50, 95% CI −4.88 to −0.11). Moreover, the overall results of these subgroup analyses were statistically significant (P<.001; Figures S12A-S12C in Multimedia Appendix 3). These findings suggest that mean participant age represents a potential source of heterogeneity influencing scores on the SNAP-IV-PI subscale and the BRIEF. Although heterogeneity was substantially reduced in the adolescent subgroup for the BRIEF (I²=0%), heterogeneity remained substantial in the preschool and school-aged children subgroups, indicating that the moderating effect of age on executive function outcomes may be primarily concentrated in adolescent populations. For the SNAP-IV-PHI subscale, heterogeneity was not substantially reduced in any subgroup after stratification by age (I²>50% in all subgroups), suggesting that age is not a primary source of heterogeneity for this outcome dimension (see Figures S12A-S12C in Multimedia Appendix 3).

Given the higher prevalence of ADHD in male children and adolescents, studies in which the proportion of female participants reached 30% were defined in this study as the group with a notable proportion of female participants. Accordingly, in the subgroup analyses based on sex ratio, studies were categorized into a male group (proportion of male participants >70%) and a female group (proportion of female participants ≥30%). After stratification by sex ratio, the results of subgroup analyses for all outcome measures indicated that sex ratio did not emerge as a potential source of heterogeneity (see Figures S13A-S13C in Multimedia Appendix 3).

To evaluate the robustness of the pooled results, sensitivity analyses were conducted using the leave-one-out method. The results revealed that for the SNAP-IV-PI subscale, the pooled effect size changed substantially after excluding the study by Zheng et al [50], suggesting that this study exerted a dominant influence on the outcome for this measure. Similarly, for the SNAP-IV-PHI subscale, the stability of the pooled results was affected following the exclusion of the study by de Oliveira Rosa et al [61]. For the BRIEF, the exclusion of the study by Hilton et al [64] also had a substantial impact on the overall effect size. These findings indicate that these particular studies represent potential sources of the high heterogeneity observed in the corresponding outcome measures. This influence may be attributable to the relatively small sample sizes of these studies (all with group sample sizes <30), which could lead to disproportionate weighting in the pooled analyses and consequently contribute to increased heterogeneity (see Figures S14A-S14C in Multimedia Appendix 3).

To assess whether the SUCRA-based ranking of AI-integrated cognitive-motor dual-task DTx as the top modality was robust to the inclusion of studies with a high risk of bias, we conducted a sensitivity analysis excluding the high-risk-of-bias studies, the results of which are presented in Multimedia Appendix 3 (Figures S15A-S15D). In this analysis, AI-integrated cognitive-motor dual-task DTx remained the highest-ranked intervention across all outcomes, consistent with the primary analysis, indicating that the SUCRA-based ranking of this modality as the optimal intervention is robust to the exclusion of high-risk-of-bias studies.

Funnel plots and Egger test were used to evaluate small-study effects. Assessments were performed for outcome measures with more than 10 included studies, specifically the ADHD-RS and BRIEF. No obvious asymmetry was observed in the funnel plots for either outcome. Egger test revealed no significant evidence of small-study effects for studies using the ADHD-RS (P=.76) or the BRIEF (P=.38) as outcome measures (all P>.05; see Figure 12).

For the ADHD-RS and SNAP-IV (both the PI and PHI subscales), the certainty of evidence comparing various DTx modalities with conventional interventions was rated as low. In contrast, for the BRIEF, the certainty of evidence was rated as moderate. These GRADE ratings indicate that the findings of this study should be interpreted with caution (see Table 1).

SUCRA rankings consistently placed AI-integrated cognitive-motor dual-task DTx first across the ADHD-RS and both SNAP-IV subscales, with statistically significant advantages over both nonpharmacological and pharmacological conventional treatments. For the ADHD-RS, the effect relative to nonpharmacological therapy exceeded the established minimal important difference (MID) threshold of 4 points [75]. The advantage over medication did not reach this threshold; moreover, this comparison relies on indirect evidence and should be interpreted cautiously [75]. Notably, the modality showed a particularly pronounced benefit on hyperactivity-impulsivity symptoms, with a substantially greater magnitude of improvement than other DTx modalities—a domain where conventional nonpharmacological interventions typically produce only small to moderate effects [36].

The superior performance of this combined modality likely reflects synergies between cognitive-motor dual-task design and AI-driven personalization [11,76]. From the perspective of task design, this dual-task paradigm possesses a unique neurophysiological theoretical foundation compared to traditional single-task training. According to Klingberg et al [11], the dual-task paradigm requires the brain to coordinate motor output (eg, balance control and fine motor skills) while simultaneously executing cognitive tasks (eg, attentional control and working memory updating) [11]. Although speculative, this high-intensity cognitive load may more effectively activate frontostriatal circuitry and influence dopaminergic neurotransmission, thereby potentially enhancing neuroplasticity [11,76]. However, the present study did not directly measure neural activity or neurotransmitter function, and this mechanistic interpretation remains speculative. Future neuroimaging studies (eg, functional magnetic resonance imaging) are needed to test these hypothesized mechanisms.

From the perspective of AI empowerment, AI-integrated DTx leverage machine learning algorithms to analyze patients’ task performance indicators in real time (eg, reaction time, accuracy rates, and attentional fluctuation patterns) and dynamically adjust task difficulty and training content accordingly [77]. This may help patients remain within an optimal training zone where their capabilities are appropriately challenged, potentially maximizing training benefits [8,14]. The study by Bilan et al [14] demonstrated that AI-driven adaptive algorithms significantly enhance treatment adherence and the magnitude of cognitive improvement in children with ADHD. All DTx modalities also incorporate game-based elements (eg, points, levels, rewards, and narrative contexts) as supportive components. Although game elements are not considered direct therapeutic agents, they play a critical role in enhancing user engagement, motivation, and treatment adherence, particularly in pediatric populations [78]. The present study extends this understanding by suggesting that, during dual-task execution, AI algorithms may identify cognitive bottlenecks (eg, periods of attentional lapses) and dynamically adjust task parameters to target these vulnerable areas, thereby potentially facilitating more precise modulation of neural circuits [13]. However, this hypothesized mechanism remains to be empirically verified, and future neuroimaging studies are needed to test these hypotheses.

For executive functions measured by the BRIEF, AI-integrated cognitive-motor dual-task DTx also achieved the highest SUCRA ranking and significantly outperformed both conventional nonpharmacological and pharmacological controls.

Executive function is a multidimensional construct encompassing inhibitory control, working memory updating, and cognitive flexibility [79]. Single-task DTx typically target isolated cognitive domains, limiting their capacity for broad transfer to real-world executive function [80]. In contrast, cognitive-motor dual-task training inherently requires coordinated deployment of multiple executive subcomponents, mirroring the cognitive demands of daily functioning [81]. This capacity for multitask coordination is itself a critical manifestation of executive functions [82]. According to the executive function development theory of Diamond [83], training with higher ecological validity produces stronger and more generalizable transfer effects. Cognitive-motor dual-task training parallels real-life situations such as “walking while thinking,” and this dual-task paradigm may produce broader transfer effects by promoting the integrated training of executive function subcomponents [84]. One potential mechanism underlying this broader transfer is that dual-task training may enhance the connectivity between prefrontal regions and motor-related cortical areas, thereby facilitating the integration of cognitive and motor processes [85]. However, this mechanistic interpretation remains speculative in the absence of direct neurophysiological evidence from the present study.

The integration of AI further amplifies this advantage. The AI-integrated cognitive-motor dual-task DTx modalities included in this study (eg, AKL-T01, BrainFit, and SDT-001) all use AI-driven adaptive algorithms capable of dynamically adjusting cognitive task difficulty and motor task complexity based on patients’ real-time performance [10,12,67]. Beyond the general adaptive adjustment described earlier, a possible mechanism by which AI integration contributes to executive function enhancement is that adaptive algorithms may continuously calibrate the task cognitive workload to match individual fluctuating attention and working memory capacity, thereby preventing cognitive overload or under-engagement [13]. Nevertheless, this hypothesis awaits direct testing in future studies using neuroimaging or electrophysiological measures.

When interpreting the findings of this NMA, 3 methodological factors should be considered simultaneously: heterogeneity, risk of bias, and certainty of evidence.

PI-based heterogeneity assessments revealed differential generalizability across outcome measures. The PI for the ADHD-RS were consistently narrow and excluded zero, indicating that the improvements in core ADHD symptoms are robust and reproducible. In contrast, the PI for both the SNAP-IV (PI and PHI subscales) and the BRIEF all crossed zero, suggesting that improvements in inattention, hyperactivity-impulsivity, and executive functions may vary considerably across populations, thus exhibiting limited generalizability to individual patients. Subgroup and sensitivity analyses further identified intervention duration, age, and several small-sample studies as potential sources of heterogeneity; however, the intervention rankings based on SUCRA values remained consistent. Collectively, these findings indicate that AI-integrated cognitive-motor dual-task DTx represents a statistically significant average benefit (a central tendency) rather than a universally fixed therapeutic effect.Therefore, when tailoring individual clinical care, practitioners should consider patient-specific factors such as age and treatment duration.

Regarding risk of bias, 40.6% of the included RCTs were rated as having a high risk of bias, primarily due to inadequate reporting of randomization methods or the inability to blind parents as outcome assessors. A sensitivity analysis excluding the high-risk-of-bias studies confirmed that AI-integrated cognitive-motor dual-task DTx remained the highest-ranked intervention across all outcomes, consistent with the primary analysis, indicating that the SUCRA-based ranking of this modality as the optimal intervention is robust to bias exclusion.

Regarding GRADE certainty, the evidence for ADHD-RS and SNAP-IV outcomes was rated as low certainty, whereas the evidence for the BRIEF was rated as moderate certainty. The low ratings were primarily driven by serious imprecision (wide CI crossing the null for some comparisons) and a high risk of bias in some included studies. These GRADE ratings indicate that the findings should be interpreted with caution.

In summary, while the SUCRA-based rankings consistently favored AI-integrated cognitive-motor dual-task DTx across all outcomes, the strength of this evidence is constrained by low to moderate GRADE certainty, substantial heterogeneity in some outcomes, and a notable proportion of studies with a high risk of bias. The absolute effect estimates should therefore be interpreted with the above limitations in mind.

These findings have several important clinical implications and should be considered within a human-centered digital health framework[86]. When conditions permit, AI-integrated cognitive-motor dual-task DTx may be considered as a nonpharmacological intervention option for children and adolescents with ADHD, particularly for those with prominent hyperactivity-impulsivity symptoms or those who experience adverse effects from pharmacotherapy. Notably, however, this conclusion is based on probabilistic SUCRA rankings, and the differences between this modality and other DTx modalities did not reach statistical significance across several outcome dimensions. Therefore, clinical decisions should integrate individual patient factors, including age, symptom profile, comorbidities, family preferences, and intervention accessibility[86].

DTx should be viewed as supportive rather than substitutive components of comprehensive ADHD care[86]. They are most effective when integrated into a multimodal treatment plan that may include pharmacotherapy, behavioral therapy, and educational support[86]. Successful implementation requires careful consideration of usability, engagement, and family acceptability [87].

Clinical oversight and governance are equally critical for the safe and effective use of DTx in pediatric populations [88]. Health care providers should monitor treatment progress, adherence, and potential adverse effects and adjust the treatment plan as needed [88]. Clear protocols for responsibility assignment, outcome documentation, and family communication should be established when integrating DTx into routine clinical care pathways.

Moreover, the SUCRA advantage of AI-integrated cognitive-motor dual-task DTx must be interpreted with attention to within-category heterogeneity, as this aggregated modality spans multiple technological implementations with distinct mechanisms of action [10,12,13,52,66,68-71]. Without head-to-head comparisons across subtypes, whether this ranking reflects a general property or is subtype driven remains unclear. Beyond outcome-level effect sizes, evaluating the AI layer itself, including adaptive difficulty adjustment, real-time performance analytics, and personalized feedback, requires component-specific methodological frameworks [89]. Similarly, translating screen-based pediatric interventions into routine clinical care calls for regulatory approaches that address not only clinical efficacy but also data privacy, algorithmic transparency, age-appropriate design, and commercial incentives [90]. These considerations should inform future implementation strategies as AI-enabled DTx move from controlled trials to real-world practice.

Several limitations should be acknowledged. First, 40.6% of included studies had a high risk of bias, mainly due to inadequate reporting of randomization and blinding procedures, although sensitivity analyses suggested limited impact on overall rankings. Second, within-modality heterogeneity in AI algorithms, delivery platforms, and training protocols may reduce the precision of pooled effect estimates. Third, the relatively small number of AI-integrated DTx studies limits statistical power and introduces potential publication bias risk. Fourth, reliance on parent-reported outcomes introduces potential expectancy bias and may not fully capture school-based or objective cognitive performance. Fifth, subgroup analyses by ADHD subtype could not be performed due to insufficient reporting of outcomes stratified by diagnostic subtype in the included studies [91]. Sixth, small-study effects could not be formally assessed for SNAP-IV subscales due to the limited number of studies. Seventh, insufficient data on adherence and long-term follow-up prevented the evaluation of dose-response relationships and durability of effects. Eighth, trial conditions may not fully reflect real-world implementation factors such as family support, device access, and connectivity. Additionally, some degree of misclassification cannot be excluded given the variation in AI algorithms and delivery formats across studies, which may add uncertainty to network estimates.

Future large-scale head-to-head RCTs should compare AI-integrated DTx against pharmacotherapy and behavioral therapy using standardized outcomes. Mechanistic studies (eg, functional magnetic resonance imaging, magnetoencephalography, and electroencephalography) should validate the synergistic hypothesis. Prediction models are needed to identify patient characteristics (eg, age, sex, and ADHD subtype) predicting differential response. Pragmatic trials should assess real-world effectiveness, including family support, device access, and clinical oversight. Implementation research should examine integration strategies for DTx into pediatric ADHD care, including responsibility assignment and outcome documentation [88]. Human-centered design studies should assess usability and acceptability among children, adolescents, and families. Finally, extended follow-up (≥6 months) should determine the long-term maintenance of DTx effects on academic achievement and social functioning.

This dual-dimension classification framework NMA advances the evidence base for ADHD DTx by systematically comparing 4 modalities and integrating ranking, heterogeneity quantification via PI, and GRADE certainty assessment. AI-integrated cognitive-motor dual-task DTx emerges as the highest-ranked intervention for both core symptoms and executive functions, with preliminary evidence of synergy between dual-task design and AI personalization and with intervention duration and age identified as potential sources of heterogeneity. Despite low to moderate evidence certainty and remaining methodological limitations, these findings provide actionable guidance for clinical practice and future DTx development, pending confirmation from well-designed head-to-head trials.