This systematic review was conducted in accordance with the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) guidelines [35], using the PRISMA 2020 checklist (Checklist 1). Additionally, the study protocol was registered with the International Prospective Register of Systematic Reviews (CRD420251135302).

This systematic search was conducted in strict accordance with the PRISMA-S (Preferred Reporting Items for Systematic Reviews and Meta-Analyses search extension) guidelines [36]. A systematic search was performed across 5 major databases: PubMed (NCBI), Embase, Cochrane Library (Wiley), Web of Science, and Ovid MEDLINE. The search encompassed the period from the inception of each database to July 10, 2025, with no restrictions imposed on language or publication date. To ensure the inclusion of the most recent evidence, the search was updated on January 9, 2026. This updated search featured an optimized combination of MeSH (Medical Subject Headings) and keywords, which was informed by previous studies [27,29,30] and tailored to the characteristics of each database, thereby yielding search strategies that differed from those used initially. It should be noted that the search strategies used have not been formally peer-reviewed.

To enhance the comprehensiveness of the retrieval process, the reference lists of pertinent systematic reviews and their included studies were meticulously reviewed. In instances where essential data were absent from the included studies, we reached out to the corresponding authors via email to request the unreported yet crucial original data. The literature search was restricted to the methodologies outlined above, and gray literature, unpublished studies, and preprints were not systematically explored. All database searches were completed on January 11, 2026. Comprehensive search strategies for each database are documented in Multimedia Appendix 1.

Two authors independently conducted the screening and selection of studies according to predefined criteria. Any discrepancies encountered were resolved through discussion or, if necessary, by consulting a third reviewer. The determination of study eligibility was guided by the PICOS (Population, Intervention, Comparison, Outcomes, and Study Design) framework.

The inclusion criteria were as follows: (1) participants were aged ≥60 years and carried a diagnosis of frailty or sarcopenia, established according to specified diagnostic criteria. (2) The intervention implemented was a DHI delivered via digital platforms or technologies, through one or more modalities, including but not limited to telephone, video, mobile apps, or wearable devices. (3) Control groups received nondigital interventions, including but not limited to usual care, waitlist, active control, or blank control. (4) The outcomes associated with frailty and sarcopenia were evaluated through comprehensive assessments of muscle strength, muscle mass, physical performance, BMI, and quality of life. Specifically, muscle mass measurements included skeletal muscle mass and the Appendicular Skeletal Muscle Mass Index (ASMI). Physical performance was assessed using various performance-based tests, including gait speed, the 6-Minute Walk Test (6MWT), the 2-Minute Walk Test (2MWT), the Five Times Sit to Stand Test (FTSST), the 30-Second Chair Stand Test (30CST), the Timed Up and Go Test (TUGT), the Short Physical Performance Battery (SPPB), and balance assessments. These outcomes were systematically measured at both baseline and the study end point using objective and subjective instruments, and they were classified as either primary or secondary outcomes. (5) The study design was randomized controlled trials (RCTs). To enhance the inclusiveness and generalizability of the review findings, we removed the original restriction of a minimum of 10 participants per intervention group, thereby avoiding unnecessary exclusion of small but methodologically rigorous RCTs that can provide valuable evidence for the evidence synthesis.

The exclusion criteria were as follows: (1) the study population was not explicitly defined as frail (using established criteria such as the Clinical Frailty Scale [37], Fried Phenotype [2], etc) or sarcopenic (using diagnostic guidelines such as EWGSOP (European Working Group on Sarcopenia in Older People) [5], AWGS (Asian Working Group for Sarcopenia) [38], etc), and participants were aged younger than 60 years. (2) Studies using digital devices only for passive monitoring without a structured intervention. (3) The control group received DHIs. (4) No quantitative outcomes related to frailty or sarcopenia (eg, muscle strength, muscle mass, physical performance, and activities of daily living) were reported. (5) The data were incomplete or were presented in a format (eg, medians without IQRs) that made it impossible to calculate effect sizes. (6) Reviews, commentaries, news, conference abstracts, case reports, conference papers, or unpublished manuscripts

The literature screening was conducted using EndNote software (Clarivate). Two researchers initially screened articles by reviewing titles and abstracts, removing duplicates. If relevance could not be determined from the title or abstract, the full text was assessed. All disagreements were resolved through discussion, with the corresponding author making the final decision when consensus was not reached.

We strictly adhered to the guidelines outlined in the Cochrane Handbook for Systematic Reviews of Interventions, designed and optimized a structured data extraction form, and validated its reliability and reproducibility through preextraction in a subset of included studies. Subsequently, 2 independent researchers extracted the following information from all included studies: basic study characteristics (first author, year of publication, country or countries in which the studies were conducted, and study design), disease and diagnostic details (patient population and diagnostic criteria), participant characteristics (sample size, age range, and gender distribution), intervention and control specifics (type of digital health technology, control intervention, and duration of intervention), as well as outcome measures and intention-to-treat (ITT) analysis. Upon completion of data extraction, a third researcher verified the extracted data.

Data extraction followed the predefined criteria below: (1) for studies with multiple publications, the most recent version with the most comprehensive methodological descriptions and outcome reports was prioritized. (2) For multiarm RCTs, data from each intervention arm were extracted independently. (3) In case of missing key outcome data, the corresponding author of the original study was first contacted via email to attempt data acquisition. If data remained unavailable, the study was excluded from subsequent meta-analyses. (4) Immediate data from the first assessment after intervention completion were prioritized for extraction, with supplementary follow-up data retrieved to support comparative analyses. (5) For studies reporting both ITT analysis and per-protocol analysis, the former was used as the primary data source. (6) When the original literature did not directly report means and SDs, we used meta-analytical tools for data estimation and conversion to perform the necessary transformations or calculations [39]. All extracted data underwent final review by a third researcher.

Additionally, to systematically present the diversity of digital health interventions, 2 researchers classified the interventions using an inductive approach based on the full-text content of the included studies. Discrepancies arising during the classification process were resolved through consensus after discussions involving a third researcher.

Risk of bias was assessed using the revised Cochrane Risk of Bias tool (RoB 2.0), which covers 5 domains: randomization, deviations from interventions, missing data, outcome measurement, and result selection. Two reviewers independently assessed studies, resolving disagreements via discussion. Overall risk of bias was rated as low, some concerns, or high: low if all domains were low risk; some concerns if at least one domain had concerns and none were high risk; high if any domain was high risk or multiple domains had concerns.

The quality of evidence for each meta-analysis was appraised using the Grading of Recommendations, Assessment, Development and Evaluations (GRADE) approach [40]. Evidence quality was evaluated based on 5 downgrading factors: risk of bias, inconsistency, indirectness, imprecision, and publication bias, as well as 3 upgrading factors: effect size, impact of plausible confounding, and dose-response relationship. Evidence quality was categorized into 4 levels: high, moderate, low, and very low. Two authors independently performed the GRADE assessment with the GRADEpro GDT tool (GRADE Working Group), with discrepancies resolved by a third author.

Although the original protocol planned to use Review Manager 5.3 software (Cochrane Collaboration) and model selection based on I² statistic and Q test P values, the final data analysis was performed in RStudio (Posit, PBC). A conservative random-effects model, grounded in conceptual assumptions regarding between-study heterogeneity, was used. Effect sizes were pooled using the Hartung-Knapp-Sidik-Jonkman (HKSJ) method [41]. To strengthen methodological rigor and clinical interpretability, additional analytical methods beyond the original protocol were implemented during the analytical refinement phase, including 95% prediction intervals (PIs) and heterogeneity quantification using τ².

This systematic review calculated pooled effect sizes using the changes in means and SDs from pre- to postintervention, with the SD of change scores estimated using the equations specified in the Cochrane Handbook for Systematic Reviews of Interventions. The calculations were performed as follows:

Here, r represents the correlation coefficient between pre- and postintervention values. If this correlation coefficient was not reported in the original studies, a value of r=0.5 was assumed, consistent with the Handbook’s recommendations. When studies provided only between-group differences, the corresponding authors were contacted to obtain within-group change data. In instances where SEs were reported instead of SD, the SD was calculated using the formula:

SD=SE×n

When data were reported as median (IQR), the mean and SD were derived using the sample size–based method described by Hozo et al [42]. Studies that did not report SD, SE, or 95% CI and for which the corresponding authors did not provide these values upon request were excluded from the meta-analysis. Additionally, when outcomes were stratified by sex, age, or body weight status, they were analyzed separately by subgroup.

For outcome measures assessed with identical instruments and units, the weighted mean difference (WMD) was applied to pool effect estimates; for those evaluated using different instruments or scales, the standardized mean difference (SMD) was used to ensure comparability of effect sizes. Given the predominantly small sample sizes across the included studies, Hedges g was selected as the estimator for SMD to correct for small sample bias. Following the Cochrane Handbook, SMD values of 0.2, 0.5, and 0.8 were interpreted as representing small, medium, and large effects, respectively. For multiarm trials, the shared control group was split into approximately equal subgroups, with one subgroup assigned to each intervention arm for comparison, thereby avoiding double counting of participants and preventing unit-of-analysis errors [43,44]. For cluster RCTs, we first evaluated whether the original studies used appropriate statistical methods to account for intracluster correlation [45]. Where such appropriate adjustments were absent from the original reports, an inflated SE approach was applied to approximate a corrected analysis.

To quantify the real-world variability of the intervention effect across different populations and application scenarios, the study also reports PIs [46]. Because conventional PIs perform poorly when the number of studies is small or heterogeneity is low, we used the bootstrap method proposed by Nagashima et al [47] to calculate PIs. This approach draws samples of the heterogeneity parameter τ² from the exact distribution of the Cochran Q statistic and combines them with the Hartung-Knapp SE to construct a predictive distribution, thereby improving the robustness of PI estimation and inference even when the number of studies is very limited (K<5) or heterogeneity is moderate. In addition, the Minimal Clinically Important Difference (MCID) reported in previous literature in the field was referenced to evaluate the clinical relevance of the estimated effects.

Given the noticeable differences among the included studies in participant characteristics, intervention protocols, and adherence, a conservative random effects model was chosen based on the conceptual assumption of a distribution of true effects [48]. For effect size pooling, following the recommendation of the Cochrane Collaboration, we used the HKSJ method for random-effects meta-analysis. By adopting a distribution and adjusting the SE with the Q statistic, the HKSJ approach yields more robust CIs for the effect size compared with the conventional DerSimonian-Laird method, especially when the number of included studies is small and statistical power is limited; it thus better accounts for the inherent uncertainty and imprecision in effect estimation [41]. Restricted maximum likelihood estimation was used to estimate the between-study variance τ² so as to more accurately reflect the impact of heterogeneity on the effect estimates. Heterogeneity was assessed using the Q-test, I² statistic, and τ² metric [49]. When 3 or more studies are included, we also report 95% PIs to indicate the expected distribution range of effect sizes in new settings. The I² statistic is reported for comparability with other studies but is interpreted with caution [49,50]. All statistical analyses were performed using R software (version 4.5.2; R Core Team) within the RStudio environment.

When 10 or more studies were available, small-study effects were assessed using funnel plots and the Egger test, which were treated as indicators of such effects rather than sole evidence of publication bias [51,52]. To systematically investigate potential effect modifiers, subgroup analyses were conducted for intervention duration (≤8 wk vs ≥12 wk), control type (exercise vs nonexercise), intervention type, implementation mode (home or remote vs center-based), and synchronization mode (synchronous vs asynchronous). A subgroup was not analyzed if it contained fewer than 4 included studies. All subgroup findings are exploratory and do not imply causality. These subgroup analyses were not specified in the preregistered protocol. All outcomes reported align fully with the preregistered protocol. Sensitivity analysis was performed using the leave-one-out method to evaluate the robustness of the pooled effect estimates. When 10 or more studies were included, funnel plots and the Egger test were used to assess small-study effects; it should be noted that these methods are designed primarily to detect small-study effects rather than to serve as conclusive evidence of publication bias [53,54].

In the initial systematic database search, a total of 3506 studies were identified. After the removal of 1895 duplicate entries, 1611 studies remained. Following title and abstract screening, 97 articles underwent full-text review. After full-text assessment, 81 studies were excluded for the following reasons: unavailable full text (n=31), lack of focus on sarcopenia or frailty (n=18), inconsistent intervention measures (n=15), differing outcome indicators (n=8), nonrandomized study design (n=5), and unobtainable or nonconvertible data (n=4). Ultimately, 16 studies met the inclusion criteria for the final analysis [55-70]. The detailed screening process is shown in Figure 1.

This analysis included 16 studies [55-70] involving 1109 participants from 3 geographic regions, with sample sizes ranging from 15 to 201. The geographical distribution of the studies was as follows: 9 studies were conducted in China [55,57,59-62,64,65,70], 2 studies in Korea [63,69], and one each in the United States [56], England [67], and Thailand and Spain [58]; one additional study was a multicenter trial conducted across Italy, Germany, Austria, Spain, England, Belgium, Sweden, Japan, Korea, and Australia [66]. All were RCTs completed between 2012 and 2025. Four trials used a 3-arm design [55,56,63,65], one a 4-arm design [57], and the rest a 2-arm design [58-62,64,66-70]. Seven studies focused on frailty [56,58,60,61,63,66,70], 8 on sarcopenia [55,57,59,64,65,67-69], and 1 on both [62]. Most compared DHIs with control conditions such as usual care, health education, or nondigital exercise.

DHIs mainly included apps, artificial intelligence, virtual reality, exergames (such as those using Kinect and Nintendo Wii), health intervention platforms, wearable devices, and hybrid DHIs. These were implemented in diverse settings such as hospitals, community health centers, and senior day care centers. The duration of interventions across studies varied considerably, ranging from as short as 4 weeks to as long as 12 months. The intervention frequency was most often 2‐3 sessions per week, each lasting 20‐60 minutes. Outcome measures included muscle mass, muscle strength, physical performance, and quality of life. Detailed study and population characteristics are in Table 1.

The results of the risk of bias assessment are shown in Figure 2. Six were rated as high risk of bias [55-57,65-67], 6 as some concerns [58-60,63,64,68], and 4 as low risk of bias [61,62,69,70]. In Domain 1 (randomization process), 1 study used sequential enrollment for allocation [66] and 2 studies did not provide detailed descriptions of the randomization implementation process, with unbalanced baseline data observed [56,57], resulting in a high risk of randomization bias. In Domain 2 (deviations from intended interventions), 11 studies did not report the use of ITT analysis or modified ITT analysis [55-58,60,63-68], thus indicating some concerns regarding bias. In Domain 3 (missing outcome data), one study exhibited a high attrition rate without reporting specific reasons for withdrawal [51], while another study indicated that participants’ dropout might be related to their health status [55]. Both of these scenarios have raised concerns regarding the risk of bias from missing outcome data. For the remaining studies included in the meta-analysis, the number of dropouts was generally balanced between groups, and the reasons for withdrawal were unrelated to the study outcomes. Therefore, missing data are unlikely to have distorted the true effects, indicating a low risk of bias due to missing outcome data. In Domain 4 (measurement of the outcome), a total of 6 studies were assessed to have some degree of risk of bias [55,56,59,65-67]. Among them, 5 studies were rated as being at high risk of bias because they did not report whether outcome assessors were blinded, and all their outcome measures incorporated subjective assessment items [55,56,65-67]. Another study was judged to have some concerns regarding risk of bias; although it also failed to report the implementation of blinding, all its outcome measures were objective assessments [59]. In Domain 5 (selection of the reported result), all but one study [57] was consistent with their prepublished protocols.

In GRADE assessments, overall certainty across all comparisons and outcomes is very low to low due to combinations of risk of bias, inconsistency, and imprecision (Multimedia Appendix 2).

Six studies [55,62,65-67,69] assessed quality of life. Following the splitting of shared control group sample sizes from multiarm trials [55,65], 8 study arms were included in the analysis. Pooled results indicated a small but significant improvement in quality of life with DHIs compared to the control group (SMD 0.16, 95% CI 0.05-0.27, 95% PI 0.04-0.28; τ²=0; P=.97; Figure S18 in Multimedia Appendix 3). The 95% CI did not cross zero, confirming statistical significance. No heterogeneity was observed across studies (I²=0%). Similarly, the 95% PI did not cross zero, suggesting that the direction of the beneficial effect is likely to remain consistent in future studies or different populations. However, caution is warranted as the reliability of this 95% PI may be limited by the small number of included studies. Due to risk of bias and imprecision, the quality of evidence regarding the effect of DHIs on QoL was rated as “low” (Multimedia Appendix 2).

Three studies [57,59,67] evaluated BMI. By dividing the sample size of the shared control group in a multiarm trial [57], 5 study arms were ultimately included for analysis. The pooled analysis showed that DHIs did not significantly improve BMI compared with control (WMD 0.09, 95% CI –0.36 to 0.53, 95% PI –0.85 to 1.04; τ²=0.07; P=.16; Figure S19 in Multimedia Appendix 3), despite moderate heterogeneity (I²=38.6%). The 95% CI included zero, indicating that the mean intervention effect was not statistically significant. The 95% PI also included the null value, indicating that DHIs could be ineffective or even harmful in future research or other populations. Owing to the small number of included studies, the robustness of this 95% PI should be viewed as restricted. Given the nonsignificant effect of the intervention on BMI and the limited number of studies, no GRADE assessment or subgroup analysis was performed for this outcome.

We conducted small-study effect analyses using funnel plots combined with Egger regression test for outcome measures with at least 10 study arms included. Funnel plots (Figures S1-S4 in Multimedia Appendix 6) were constructed to visually explore potential asymmetry. Visual inspection revealed no marked asymmetry in the funnel plots for any outcome measure. Egger test results indicated no significant small-study effect for any outcome: grip strength (P=.92), ASMI (P=.54), gait speed (P=.59), or TUGT (P=.47). It should be noted that observed funnel plot asymmetry may not only reflect publication bias but could also arise from between-study heterogeneity, random error, or methodological differences. Therefore, the P values from Egger test in this study serve only as an indicator of potential small-study effects and should not be interpreted as definitive evidence of publication bias. This is especially relevant given the limited number of studies included, as these biases may remain undetected due to insufficient statistical power.

This study has several limitations. First, although the search strategy did not restrict language, only English-language publications were ultimately included, which may introduce language bias and reduce the applicability of the findings to non–English-speaking contexts. Second, only RCTs were selected to ensure methodological rigor, which may have excluded non-RCT evidence relevant to the real-world implementation and long-term feasibility of digital health tools. Third, most included studies were conducted in China, limiting the applicability of the results to other health care systems and cultural settings. Finally, substantial heterogeneity in outcome measures and control conditions across studies complicates result synthesis and limits the clarity of conclusions regarding DHI effectiveness. Future research should address these limitations through high-quality, multicenter, and cross-cultural clinical trials to verify the effectiveness of DHIs and clarify their optimal implementation models.

While the overall certainty of evidence remains limited, DHIs have the potential to serve as a scalable and patient-centered complement to traditional rehabilitation methods for individuals experiencing frailty and sarcopenia. To facilitate the integration of DHIs into existing health care systems, clinicians should consider providing structured support across 3 critical domains: accessibility, user engagement, and technical literacy. Regarding accessibility, DHIs should be thoughtfully integrated into clinical pathways, with particular attention given to patients facing functional limitations, mobility challenges, or residing in remote locations, thereby helping to mitigate geographical and physical barriers. Furthermore, the establishment of regular follow-up procedures may aid in addressing ongoing usability concerns and in evaluating sustained outcomes. To improve patient engagement, it is advisable to recommend high-interactivity tools, such as exergames, that align with individual patient interests. For older adults, DHIs should prioritize senior-friendly features, including simplified interfaces and voice assistants, to minimize barriers and enhance adherence. In terms of technical literacy, clinical teams should develop proficiency in the operation of these tools and in providing patient guidance through comprehensive training programs. Initial support in digital health literacy should be extended to patients, while family members or caregivers should be encouraged to assist individuals with limited technical adaptability, thereby ensuring the sustainability of the intervention.

This study is the first systematic review to examine the impact of DHIs on muscle function (including muscle mass and muscle strength), physical performance, and quality of life among older adults experiencing frailty and sarcopenia. The results indicate that DHIs generally surpass control conditions, resulting in improvements in muscle mass and specific physical performance measures, such as gait speed, TUGT, 30CST, and balance. Additionally, DHIs have a positive impact on quality of life. Nevertheless, these results warrant cautious interpretation. Except for quality of life, all other outcomes exhibited wide PIs encompassing the null value, indicating significant heterogeneity across studies. This variability suggests that statistically significant improvements may not be consistently observed across different populations or clinical settings. The conclusions of this review must be viewed considering its methodological limitations. The wide prediction intervals for muscle mass, gait speed, TUGT, 30CST, and balance, especially the high heterogeneity and instability in balance outcomes, limit the findings’ generalizability. Some included RCTs had methodological issues, such as blinding challenges and unclear allocation concealment, potentially leading to an overestimation of DHIs’ effects. According to the GRADE framework, the evidence quality for outcomes such as muscle mass, gait speed, TUGT, 30CST, balance, and quality of life is rated very low to low due to concerns about bias, inconsistency, and imprecision, reducing confidence in the intervention’s benefits.

Nevertheless, DHIs continue to be regarded as a viable strategy for improving the accessibility and cost-effectiveness of managing frailty and sarcopenia. These interventions are particularly valuable for addressing treatment gaps among populations that face barriers to adequate health care services, such as limited regional resources, time and transportation constraints, or physical functional limitations. Future research endeavors should prioritize the development of a standardized core outcome set for DHIs and the execution of robust, multicenter, large-scale, high-quality RCTs that include nutritional support components. These trials should also assess long-term health benefits and cost-effectiveness. Generating such high-quality evidence will facilitate the standardized application and effective integration of DHIs into the clinical management of frailty and sarcopenia, thereby establishing a foundation for their evolution into scalable and sustainable public health solutions to meet the global prevention and control requirements of these conditions.