This systematic review and meta-analysis was conducted and reported in accordance with the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 statement [34]. The protocol was prospectively registered in PROSPERO (CRD420251049015). The PRISMA 2020 checklist is provided in Checklist 1.

We included RCTs enrolling adult patients (≥18 years) undergoing TKA that compared IRR with any control intervention, including face-to-face rehabilitation, unsupervised home-based rehabilitation, usual care, outpatient rehabilitation, or inpatient rehabilitation.

IRR was defined as rehabilitation programs delivered through digital or telecommunication technologies that enabled bidirectional communication between patients and health care providers. These interventions could include synchronous modalities (eg, real-time video or telephone-based supervision), asynchronous modalities (eg, app-based programs with delayed feedback), or hybrid models combining both approaches.

We excluded nonrandomized studies, non-IRR interventions (ie, programs without clinician-patient interaction), studies involving mixed joint replacement populations without separate TKA data, and studies with insufficient data for quantitative synthesis.

Only studies published in English or Chinese were included.

We systematically searched PubMed (MEDLINE), Cochrane CENTRAL, Embase (via Ovid), Web of Science Core Collection, CINAHL, Scopus, and CNKI from database inception to May 5, 2026 (updated from the original search conducted up to May 25, 2025). In addition, the reference lists of included studies and relevant systematic reviews were manually screened to identify potentially eligible studies.

The search strategy was developed and reported in accordance with PRISMA-S (Preferred Reporting Items for Systematic Reviews and Meta-Analyses Literature Search Extension), incorporating both controlled vocabulary and free-text terms related to TKA and remote rehabilitation [35]. The search strategy was developed by 2 authors (LP and BS) and independently checked by 2 additional authors (KW and YZ) for completeness, consistency, and relevance to the review question. For database-specific searches, we used MeSH terms in PubMed, Emtree terms in Embase, database-specific subject headings where applicable, field modifiers, truncation, and a broad range of synonyms related to TKA, telerehabilitation, remote rehabilitation, digital rehabilitation, telehealth, app-based rehabilitation, virtual rehabilitation, and rehabilitation therapy. The PRISMA-S checklist is provided in Checklist 2, and the PRISMA-S Search Reporting Details and Complete Database-Specific Search Strategies checklist is provided in Checklist 3.

Two reviewers (LP and KW) independently screened records in 2 stages (title and abstract screening followed by full-text review) using EndNote (version 21; Clarivate) and Rayyan (Rayyan Systems Inc). Duplicates were removed prior to screening. Studies were assessed against predefined eligibility criteria. Disagreements were resolved through discussion or by consulting a senior reviewer.

Two reviewers (LW and YZ) independently extracted data using a standardized, pilot-tested data collection form, including study characteristics (first author, year, country, and study design), sample size, intervention and control descriptions, type of remote intervention (synchronous, asynchronous, or hybrid), intervention details, treatment duration, follow-up time points, and outcome measures (eg, pain, functional outcomes, ROM, muscle strength, mobility, general health status, and health-related quality of life).

Where necessary, data were extracted or calculated from reported statistics. For trials with multiple publications, we used the earliest report as the primary source and supplemented it with additional follow-up data from subsequent publications.

Outcomes were prespecified and categorized into domains prior to analysis. The primary outcomes included pain (eg, visual analog scale [VAS] and numeric rating scale [NRS]) and functional outcomes (eg, Western Ontario and McMaster Universities Osteoarthritis Index [WOMAC] and Knee Injury and Osteoarthritis Outcome Score [KOOS]), while secondary outcomes included ROM, quadriceps muscle strength, mobility (eg, Timed Up and Go test [TUG] and 6-minute walk test [6MWT]), general health status (36-Item Short Form Survey [SF-36]), and health-related quality of life (EQ-5D). Outcomes were grouped and synthesized based on their underlying constructs and measurement characteristics. When multiple studies assessed the same construct using comparable or transformable scales (eg, pain measured by VAS or NRS), results were pooled. In contrast, outcomes representing distinct domains (eg, patient-reported function, mobility, general health status, and health-related quality of life) or measured using instruments with substantially different conceptual frameworks (eg, WOMAC, KOOS, TUG, and 6MWT) were analyzed separately to preserve clinical interpretability and avoid inappropriate aggregation.

Outcomes were analyzed at predefined follow-up intervals: short-term (≤6 weeks), mid-term (>6 weeks to ≤3 months), and long-term (>3 months). When multiple time points were reported within the same interval, the time point closest to the upper limit of the predefined interval was selected. For long-term outcomes, given the limited availability of data beyond 12 months, the time point closest to 6 months was preferentially selected to ensure comparability across studies and to capture clinically stable treatment effects. A single time point per category was selected to avoid double counting.

Risk of bias was assessed independently by 2 reviewers (LP and BS) using the Cochrane Risk of Bias 2 tool across 5 domains: bias arising from the randomization process, bias due to deviations from intended interventions, bias due to missing outcome data, bias in measurement of the outcome, and bias in selection of the reported result [36].

We performed meta-analyses using R (version 4.0.0; R Foundation for Statistical Computing). For continuous outcomes, mean difference (MD) or standardized mean difference (SMD) with 95% CIs were calculated, depending on the measurement scales used. For dichotomous outcomes, risk ratios with 95% CIs were calculated. In addition, outcome measures were synthesized based on their underlying constructs. When multiple instruments assessed a similar construct and were considered conceptually comparable, results were pooled using SMD. In contrast, outcomes representing distinct domains or measured using instruments with different conceptual frameworks (eg, patient-reported function vs performance-based mobility) were analyzed separately to preserve clinical interpretability and avoid inappropriate aggregation.

Between-study heterogeneity was assessed using the I² statistic and interpreted in conjunction with clinical and methodological considerations. A random-effects model was applied to all meta-analyses to account for expected between-study variability [37]. For random-effects analyses, 95% prediction intervals (PIs) were additionally calculated to estimate the range of true effects across different settings [38]. CIs were interpreted as reflecting uncertainty around the pooled average effect, whereas PIs were interpreted as reflecting the expected distribution of true effects across comparable clinical settings [38,39]. PIs were calculated using the confidence distribution approach proposed by Nagashima et al [39] to improve interval estimation in random-effects meta-analysis, particularly when the number of included studies was small.

For outcomes with a small number of studies, the Hartung-Knapp-Sidik-Jonkman (HKSJ) method was used to provide more robust estimates [40]. Sensitivity analyses were conducted by excluding studies judged to be at high risk of bias. Small-study effects and potential publication bias were assessed using funnel plots and the Egger test when at least 10 studies were available [41]. When the number of included studies was insufficient (eg, fewer than 10 studies for publication bias assessment or limited data for subgroup analysis), these analyses were not performed [42]. A narrative synthesis was conducted when meta-analysis was not feasible. To avoid unit-of-analysis errors, we ensured that each study contributed independent participant data and that no double counting occurred across comparisons [43].

The certainty of evidence for each outcome was assessed using the GRADE (Grading of Recommendations Assessment, Development and Evaluation) approach [44]. The overall quality of evidence was evaluated across studies, considering risk of bias, inconsistency, indirectness, imprecision, and publication bias.

Each outcome was rated as high, moderate, low, or very low certainty. The assessment was conducted independently by 2 reviewers, with disagreements resolved through discussion or consultation with a senior reviewer.

A total of 5154 records were identified through database searches, including PubMed (n=876), CENTRAL (n=1010), Embase via Ovid (n=1730), Web of Science (n=395), CINAHL (n=126), Scopus (n=931), and CNKI (n=86). An additional 12 records were identified through manual screening of reference lists.

After removal of 2289 duplicates, 2865 records remained for title and abstract screening. Of these, 2639 records were excluded based on predefined eligibility criteria. The remaining 226 full-text papers were assessed for eligibility.

Among the full-text papers, 203 were excluded for the following reasons: not RCTs (n=68), absence of IRR interventions (n=73), not involving TKA or involving mixed joint populations without separate TKA data (n=27), and insufficient data for extraction (n=35).

Ultimately, 24 reports describing 23 RCTs [28-32,45-62] were included in the qualitative synthesis and quantitative meta-analysis. The PRISMA flow diagram of the study selection process is presented in Figure 1.

The included RCTs were published between 2003 and 2025, with sample sizes ranging from 20 to 368 participants. Studies were conducted across Asia (China, Korea, Singapore, and Pakistan), Europe (Spain and the Netherlands), North America (the United States and Canada), and Australia, reflecting a broad international distribution. Intervention durations varied from 2 weeks to 6 months, with follow-up assessments extending to 12 months in some trials.

All included interventions were consistent with the predefined definition of IRR, involving bidirectional communication between patients and health care providers. Intervention modalities included synchronous real-time telerehabilitation (eg, videoconferencing), asynchronous platforms (eg, app-based exercise programs with delayed feedback), and hybrid approaches. Some interventions incorporated wearable sensors, motion analysis systems, or app-based monitoring.

Control groups were heterogeneous and included conventional in-person rehabilitation, unsupervised home exercise programs, outpatient rehabilitation, inpatient rehabilitation, and usual care.

Outcomes were categorized into predefined domains. Pain outcomes were commonly assessed using the VAS and NRS. Functional outcomes were evaluated using various scales, including WOMAC, KOOS, and Hospital for Special Surgery Knee Score, as well as performance-based measures such as the TUG and 6MWT. Additional outcomes included ROM, quadriceps muscle strength, general health status (SF-36), and health-related quality of life (EQ-5D), patient satisfaction, and health care use. Detailed characteristics of the included studies are summarized in Table 1.

Using the Cochrane Risk of Bias 2 tool, a total of 23 RCTs were included in the risk of bias assessment. Overall, 7 studies were judged as low risk of bias, 7 studies raised some concerns, and the remaining 9 studies were considered to have a high risk of bias.

Studies classified as having some concerns commonly lacked detailed reporting of allocation concealment, did not clearly specify assessor blinding, or had incomplete information regarding adherence to intended interventions. Studies judged to be at high risk of bias were primarily single-center trials with methodological limitations, including inadequate or unclear randomization procedures, absence of allocation concealment, lack of blinded outcome assessment, and inappropriate handling of missing data. In several cases, interventions were not strictly controlled or involved multiple components, increasing the likelihood of performance bias. The study-level traffic light plot of the domain-level and overall risk-of-bias judgments is presented in Figure 2, and the percentage-based graphical summary of the assessments is shown in Figure 3.

Publication bias (funnel plot and Egger test) and subgroup analyses were not performed due to the limited number of studies available for each outcome, which precluded reliable statistical assessment.

Across outcomes, 95% CIs were used to interpret the uncertainty around the pooled average effects, whereas 95% PIs were used to assess the potential range of true effects across comparable clinical settings. For several outcomes, the CIs indicated no statistically significant average effect, while the PIs were wide and crossed the null value, indicating that effects may differ across settings. The GRADE summary of findings table for the key outcomes is presented in Table 2, and the detailed GRADE evidence profile is provided in Multimedia Appendix 2. The certainty of evidence was generally low to very low across most outcomes, primarily due to substantial heterogeneity, wide CIs and PIs, and risk of bias in several studies. Accordingly, the pooled findings should be interpreted as uncertain estimates rather than definitive evidence of equivalence or superiority.

This systematic review and meta-analysis of 23 RCTs involving 2607 participants evaluated the effectiveness of IRR compared with conventional rehabilitation after TKA. Across the prespecified primary outcomes, IRR did not demonstrate statistically significant advantages over conventional rehabilitation for pain or patient-reported function, including WOMAC and KOOS outcomes, at short-, mid-, or long-term follow-up. Findings for most secondary outcomes were similarly neutral, with no consistent benefits observed for mobility or health-related quality of life. Among ROM outcomes, only a very small improvement in short-term active extension favored IRR, and a marginal signal for long-term active extension emerged only in sensitivity analysis; however, the magnitude and consistency of these findings were limited. A short-term improvement in quadriceps muscle strength was also observed in the primary analysis, but this effect was not robust after exclusion of studies at high risk of bias and was not maintained at later follow-up. Overall, the evidence does not indicate a consistent average benefit of IRR over conventional rehabilitation after TKA based on the pooled effects and their 95% CIs. In addition, wide PIs in several analyses suggest that the true effects of IRR may vary across different clinical settings. These findings should therefore be interpreted cautiously considering heterogeneity, risk of bias in several included studies, and the generally low to very low certainty of evidence according to GRADE.

Compared with previous meta-analyses, which primarily evaluated remote rehabilitation as a broad or technology-based category, this study focused specifically on IRR defined by bidirectional communication [14-16,18,64,65]. Many of these syntheses were published relatively early, when the available randomized evidence was still limited, and consequently included a smaller number of trials drawn largely from earlier generations of remote rehabilitation [14-16,18,64,65]. In contrast, this review incorporates a substantially updated evidence base. Among the 23 RCTs included in our analysis, 9 were published in 2024 or later and, to our knowledge, are synthesized in a meta-analysis of post-TKA IRR for the first time. This expanded body of recent evidence provides a more contemporary assessment of the effectiveness of IRR in the context of rapidly evolving digital rehabilitation technologies and care models. The earliest meta-analysis included only 4 RCTs and reported that telerehabilitation achieved comparable pain relief and greater improvements than face-to-face rehabilitation [18]. However, its conclusions were based on a limited evidence base, and one included trial used home-based rehabilitation monitored only by periodic telephone calls, which does not clearly meet the criteria for telerehabilitation or the IRR definition used in our review [66]. This may have contributed to conceptual heterogeneity and overestimation of benefit. Jiang et al [64] included 4 early RCTs and concluded that in-home telerehabilitation achieved pain control comparable to face-to-face rehabilitation and might provide better functional recovery after TKA, while also acknowledging the need for larger samples to confirm its efficacy. Tsang et al [16] included 11 RCTs and reported that telerehabilitation achieved pain and functional outcomes comparable to conventional in-person rehabilitation. Although most included interventions were consistent with remote rehabilitation, several trials involving telephone-based follow-up or home-based rehabilitation programs were also synthesized within the same evidence base [66-68]. Zhang et al [14] compared home-based telerehabilitation with hospital-based rehabilitation, focusing primarily on differences in rehabilitation setting rather than on the interactive characteristics of remote care. Another recent review focused on the needs and experiences of patients participating in remote rehabilitation rather than clinical effectiveness [65]. Moreover, it synthesized qualitative evidence from both total hip arthroplasty and TKA, making its scope and research question fundamentally different from the present TKA-specific efficacy review [65]. The most recent meta-analysis included a larger body of RCTs and suggested that remote rehabilitation may outperform face-to-face rehabilitation for selected outcomes after TKA [15]. However, it still synthesized some home-based rehabilitation interventions, did not treat interactivity as a defining feature, and pooled outcomes across different follow-up periods, which may have obscured time-dependent rehabilitation effects [15]. These interventions differ substantially from feedback-enabled IRR and may have introduced conceptual heterogeneity. Accordingly, this review adopted bidirectional patient-provider interaction as a required inclusion criterion to provide a more focused assessment of IRR after TKA.

While IRR has shown potential benefits in other clinical contexts, including geriatric postural control and neurological rehabilitation, our synthesis did not demonstrate consistent superiority over conventional rehabilitation following TKA [69-72]. These results suggest that interactivity alone may not suffice to produce uniform improvements in outcomes, and that effects likely depend on intervention design, intensity, and patient characteristics [73]. Compared with prior reviews, this approach reduces conceptual heterogeneity and provides a clearer assessment of what IRR contributes after TKA.

Taken together, these comparisons highlight the distinct contribution of this review. By focusing specifically on bidirectional interactive interventions, incorporating time-stratified analyses, and applying conservative meta-analytic methods, including HKSJ CIs and Nagashima-corrected PIs, this study provides a more focused and clinically interpretable assessment of IRR after TKA. The findings suggest that IRR may be a feasible model for extending postoperative rehabilitation support, particularly where access to in-person services is constrained, but they do not establish superiority over conventional rehabilitation.

The outcome-specific findings should be interpreted in the context of the overall absence of a consistent advantage of IRR over conventional rehabilitation. Across the primary outcomes, pain and patient-reported function, assessed using WOMAC and KOOS, did not show stable benefits favoring IRR at any follow-up period. These findings suggest that, although interactive technologies may facilitate rehabilitation delivery, they do not necessarily translate into superior symptom relief or broader self-reported functional recovery compared with established postoperative rehabilitation approaches [74].

Several secondary outcomes showed isolated signals that warrant cautious interpretation. A small short-term difference in active extension ROM favored IRR, but the magnitude of this effect was very limited and is unlikely to indicate a clinically meaningful improvement on its own. Similarly, quadriceps muscle strength showed a short-term advantage in the primary analysis, but this finding was no longer robust after exclusion of studies at high risk of bias and was not maintained at later follow-up. Mobility assessed by TUG and health-related quality of life assessed by EQ-5D did not demonstrate significant advantages for IRR, while evidence for SF-36 and 6MWT remained insufficient for firm quantitative conclusions. Taken together, these patterns suggest that IRR may produce modest benefits in selected domains of early postoperative recovery, but the current evidence does not support a consistent or durable effect across the broader spectrum of TKA rehabilitation outcomes.

The interpretation of these findings should also consider the nature of the comparator interventions. The relative effectiveness of IRR may depend not only on the interactive features of the remote program itself but also on the intensity and quality of the rehabilitation model against which it is compared [75-77]. A recent meta-analysis of pulmonary telerehabilitation similarly argued that remote rehabilitation was more likely to show favorable effects when compared with lower-intensity programs or usual care, whereas apparent advantages were attenuated when the comparator was high-intensity, face-to-face supervised rehabilitation [78]. This perspective is relevant to this review, in which control conditions range from conventional in-person rehabilitation to outpatient care, usual care, and unsupervised home exercise. Accordingly, the absence of consistent superiority for IRR should be interpreted as context-dependent rather than as evidence of universally equivalent or ineffective remote rehabilitation [79].

Importantly, the absence of demonstrated superiority should not be interpreted as evidence that IRR lacks clinical value [80]. The potential contribution of IRR may lie not only in producing better outcomes than conventional rehabilitation but also in extending access to structured postoperative support, maintaining continuity of care after discharge, and enabling remote monitoring, feedback, and communication between patients and rehabilitation professionals [80,81]. These features may be particularly relevant in contexts where in-person rehabilitation is difficult to access or sustain [82].

However, the present findings indicate that the availability of interactive technology alone is insufficient to guarantee better clinical outcomes. Whether IRR translates into meaningful clinical benefit likely depends on how interaction is operationalized, including the intensity and timing of feedback, the degree of personalization, the integration of monitoring data into clinical decision-making, and the characteristics of the patients receiving the intervention [22,73]. Emerging technologies may further reshape these interactive mechanisms [74,83]. For example, high-speed and low-latency communication infrastructure, such as 5G-enabled systems, may support more stable real-time supervision and data transmission, while AI may facilitate automated movement assessment, adaptive exercise progression, and more individualized feedback within remote rehabilitation platforms [84,85]. Future trials should therefore evaluate not only whether IRR is effective but also which technologically enabled interactive components meaningfully improve postoperative recovery after TKA [86].

This broader perspective is aligned with recent health systems evidence on rehabilitation delivery arrangements. A 2026 Cochrane overview concluded that the evidence for telerehabilitation and related rehabilitation service models remains limited and is often of low certainty and highlighted the need for future studies to evaluate organizational, implementation, and equity-related outcomes in addition to patient-level clinical effects [87]. Accordingly, IRR after TKA should be considered not only as a therapeutic intervention but also as a potentially important service-delivery model whose value may extend to continuity, accessibility, and organization of postoperative rehabilitation [88]. Face-to-face rehabilitation may remain preferable for patients who require close hands-on supervision, complex clinical assessment, or more intensive multidisciplinary support [2,13]. From a practical perspective, IRR may be particularly relevant for patients who face geographic, mobility, scheduling, or resource-related barriers to repeated facility-based rehabilitation, as it can extend structured postoperative support beyond the clinic and maintain communication with rehabilitation professionals [24,89].

Future research should therefore move beyond broad labels and adopt standardized, transparent definitions of therapeutic interactivity [90]. Trials should clearly report the specific interactive components being tested, including whether communication is synchronous, asynchronous, or hybrid; the frequency, timing, and intensity of clinician feedback; the use of monitoring data to adjust exercise prescriptions; the degree of personalization; and strategies used to support adherence [13,90,91]. In addition, subsequent studies should determine which patient groups are most likely to benefit from IRR, rather than assuming a uniform effect across all individuals undergoing TKA [13,87,91]. Beyond conventional clinical outcomes, future research should more systematically assess adherence, patient experience, satisfaction, cost-effectiveness, health care use, implementation feasibility, and equity of access [91]. Such evidence will be essential for defining the appropriate role of IRR within post-TKA care pathways and for identifying the interactive models, patient populations, and service contexts in which remote rehabilitation is most likely to provide meaningful value.

This study has several limitations. First, substantial heterogeneity persisted across studies in intervention characteristics, including duration, frequency, and technological platforms. Second, the number of trials for several outcomes was limited, reducing the precision and interpretability of pooled estimates. In addition, the I² statistic may be biased when the number of included studies is small and should therefore be interpreted with caution [92]. Third, several included studies were judged to have high risk of bias, and blinding of participants and therapists was generally not feasible, which may have influenced subjective outcome reporting. Fourth, wide PIs were observed in several analyses, indicating considerable uncertainty in the range of true effects that might be expected across different clinical settings. Finally, subgroup analyses and small-study effect assessments were not performed due to the limited number of studies for most outcomes, and cost-effectiveness and patient-reported satisfaction were not quantitatively evaluated.

This review is innovative in focusing specifically on IRR defined by bidirectional patient-provider communication, rather than treating all remote or technology-assisted rehabilitation as a single intervention category. In contrast to previous reviews, it combines this more precise conceptual framework with time-stratified outcome synthesis and conservative random-effects inference using the HKSJ method and PIs. By doing so, this study provides a clearer and more clinically interpretable assessment of the current evidence: in light of substantial heterogeneity, risk of bias, and generally low to very low certainty of evidence, IRR has not demonstrated consistent superiority over conventional rehabilitation after TKA, although it may serve as a feasible care model in settings where access to in-person rehabilitation is limited. These findings contribute to the digital rehabilitation field by clarifying both the promise and the current evidentiary limits of IRR, and they may inform clinical service planning as well as the design of future trials aimed at identifying which interactive features, patient groups, and implementation contexts are most likely to benefit.