This systematic review was conducted in accordance with the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) guidelines [30], using the PRISMA 2020 checklist (Checklist 1).

This review was registered in PROSPERO under registration number CRD420251151727. The original record was made available on September 20, 2025, and an amended record focusing on telerehabilitation for CNSLBP was made available on January 10, 2026. As the registration record was substantially amended from cognitive functional therapy to telerehabilitation, with changes in the review question, intervention definition, eligibility criteria, search sources, outcomes, and synthesis plan, this review is reported as a registered review with a subsequent major protocol amendment rather than as a fully prospective registration of the final review question. The main protocol deviations and corresponding corrective actions are reported in Multimedia Appendix 1.

Eligibility criteria were defined according to the population, intervention, comparator, outcomes, and study design (PICOS) framework (Textbox 1).

The systematic literature search was designed, conducted, and reported in accordance with the PRISMA-S (Preferred Reporting Items for Systematic Reviews and Meta-Analyses—Search Extension) guidelines [31]. The following electronic databases were systematically searched from inception to November 2, 2025, with a final update on May 8, 2026: PubMed (via National Center for Biotechnology Information), Embase (via Elsevier), Web of Science (via Clarivate), PEDro, Cochrane Central Register of Controlled Trials (via Wiley), China National Knowledge Infrastructure, Wanfang, VIP, and China Biology Medicine (via SinoMed). All databases were searched individually via their native platforms; no multidatabase platform searching was used. The search strategy generally combined MeSH terms, EMTREE terms where applicable, and free-text terms related to LBP, telerehabilitation, telemedicine, digital health, and randomized controlled trials (RCTs). RCT-related search terms were used to improve search specificity; no published validated search filter was used. The search strategies were developed de novo for this review and were not adapted from prior systematic reviews or previously published searches. The search strategies were adapted to the syntax, indexing structure, and search interface of each database. No restrictions on publication year were applied. Studies published in English or Chinese were eligible. The reference lists of all eligible studies were manually searched to identify additional relevant studies. No other online resources or study registries were searched. No study authors, domain experts, or other individuals were contacted to identify additional studies or obtain supplementary data. The search strategies were developed and internally checked by the research team but did not undergo external peer review. The complete search strategies for all databases are provided in Multimedia Appendix 2.

All retrieved records were imported into EndNote 20 (Clarivate) for reference management and duplicate removal. Duplicate records were first removed using the software’s automated duplicate detection function and then manually checked by the reviewers to identify any remaining duplicates. After deduplication, 2 reviewers (HW and YL) independently screened the titles and abstracts of all records according to the predefined eligibility criteria. Potentially eligible studies were then assessed through full-text review. Disagreements between the 2 reviewers were resolved through discussion or consultation with a third reviewer (SL).

The outcomes of interest in this study included pain intensity, kinesiophobia, and functional disability. Pain intensity was assessed using the visual analog scale and the Numerical Rating Scale, both of which are widely used tools for pain assessment in clinical practice and research and have demonstrated good reliability and validity [32,33]. Functional disability was evaluated using the Oswestry Disability Index [34]. Kinesiophobia was assessed using the Tampa Scale of Kinesiophobia, which is commonly used in populations with LBP to reflect fear of movement and related avoidance behaviors [35].

Two reviewers (HW and YL) independently extracted the main information from the included studies using a standardized data extraction form created in Excel (Microsoft Corp). In cases of disagreement between the 2 reviewers, a third reviewer (SL) was consulted for adjudication. The extracted information included general study characteristics (author, year of publication, country, and sample size), participant characteristics (sex and age), intervention characteristics, comparator characteristics, and outcome measures (pain intensity, kinesiophobia, and functional disability). For intervention characterization, we extracted the telerehabilitation modality, delivery mode, intervention components, duration, and frequency, supervision level, and feedback or monitoring methods. Comparator intensity was classified as active control or minimal or nonactive control based on the comparator definitions specified in the eligibility criteria.

For intervention characterization and exploratory subgroup analyses, supervision level was operationally classified as low, moderate, or high according to the degree, timing, and individualization of therapist involvement. Classification was performed independently by 2 reviewers (HW and YL), with disagreements resolved by a third reviewer (SL). Low supervision indicated self-directed or automated interventions without scheduled individualized therapist contact or feedback. Moderate supervision indicated scheduled asynchronous or periodic therapist contact, remote monitoring, adherence support, or individualized non–real-time feedback, but without real-time therapist supervision of each treatment session. High supervision indicated synchronous therapist-led sessions with real-time guidance, exercise correction, and individualized feedback during the intervention session. When an intervention included features across more than one category, classification was based on the highest level of therapist interaction that was consistently delivered during the intervention period.

If multiple follow-up time points were reported in an included study, data assessed immediately after the intervention (post-intervention) were preferentially extracted and pooled. When data were reported as medians and IQRs, they were converted into means and SDs using the formulas proposed by Wan et al [36] and Luo et al [37].

The methodological quality of the RCTs was assessed using the Cochrane Risk of Bias 2.0 tool (RoB 2.0) [38], which includes 5 domains and 1 overall judgment. The 5 domains are bias arising from the randomization process, bias due to deviations from intended interventions, bias due to missing outcome data, bias in the measurement of outcomes, and bias in the selection of the reported result. On the basis of responses to a series of signaling questions, each domain was judged as having “low risk of bias,” “some concerns,” or “high risk of bias.” Two independent reviewers (HW and YL) assessed the quality of each eligible study.

The quality of evidence was further evaluated using the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach, which classifies evidence into 4 levels: high, moderate, low, and very low [39]. The certainty of evidence from RCTs was initially rated as high and was subsequently downgraded based on risk of bias, imprecision, inconsistency, indirectness, and publication bias [40-44].

All extracted data were independently entered by 2 reviewers and cross-checked by a third reviewer. For continuous outcomes measured using the same scale or scales that could be converted to a common metric, mean differences (MDs) with 95% CIs were calculated. Visual analog scale scores ranging from 0 to 100 were rescaled to a 0 to 10 metric and pooled with Numerical Rating Scale scores. If outcome scales could not be harmonized, standardized mean differences were used.

As clinical and methodological heterogeneity was expected across telerehabilitation modalities, supervision levels, intervention durations, and comparator intensities, all meta-analyses were conducted using random effects models rather than selecting fixed effect or random effects models according to statistical heterogeneity alone [45,46]. Random effects models were fitted using the restricted maximum likelihood estimator with the Hartung-Knapp-Sidik-Jonkman adjustment, which has been recommended as a more robust approach than conventional DerSimonian-Laird methods, particularly when the number of studies is small [47]. Statistical heterogeneity was assessed using the chi-square test, the I² statistic, and between-study variance (τ²). As I² quantifies relative heterogeneity but does not describe the expected distribution of true effects across different clinical settings, 95% prediction intervals (PIs) were calculated for the main random-effects meta-analyses where statistically estimable and clinically interpretable [48]. PIs were calculated using the confidence distribution approach proposed by Nagashima et al [49], which accounts for uncertainty in the between-study variance. PIs were not calculated for subgroup analyses because several subgroups included a limited number of studies, which would yield unstable and difficult-to-interpret intervals. In addition, previously reported minimal clinically important difference (MCID) thresholds were referenced to evaluate the clinical relevance of the estimated effects.

For multiarm trials, all potentially eligible arms were assessed against the predefined PICOS criteria. When multiple telerehabilitation arms were eligible for an outcome-specific meta-analysis, we selected the comparison most closely aligned with the prespecified PICOS framework and avoided double-counting participants or shared comparator groups.

Sensitivity analyses were performed using the leave-one-out method to evaluate the robustness of the pooled effect estimates. Additional sensitivity analyses were conducted by excluding studies with very small sample sizes, defined as fewer than 20 participants per group, and studies judged to be at high risk of bias. When 10 or more studies were available, small-study effects were assessed using funnel plots and Egger regression tests, which were interpreted as indicators of small-study effects rather than as definitive evidence of publication bias [50]. Analyses were implemented in R (meta package; R Foundation for Statistical Computing).

To explore potential sources of heterogeneity, subgroup analyses were conducted according to comparator intensity, delivery mode, and supervision level when at least two studies were available in each relevant subgroup. Comparator intensity was categorized as active control or minimal or nonactive control based on the actual treatment components, intensity of supervision, and degree of individualization received by the control group, as specified in the eligibility criteria. Delivery mode was categorized as self-directed or asynchronous or therapist-supported or synchronous. Subgroup analyses by supervision level used the operational low, moderate, and high categories described in the data extraction section. Analyses by delivery mode and supervision level were not specified in the registered protocol or subsequent protocol amendment and were therefore considered post hoc and exploratory. As subgroup comparisons were made across trials and were not protected by the randomization structure of the original RCTs, all subgroup findings were interpreted as observational and hypothesis generating rather than as causal evidence. Interpretation was further limited by the small number of studies in several subgroups and by the nonmutual independence of comparator intensity, delivery mode, and supervision level.

A total of 5706 records were initially identified through database searching, of which 3261 (57.1%) were removed as duplicates. Following title and abstract screening, 56 (2.3%) articles underwent full-text review. After full-text assessment, 42 (75%) studies were excluded for the following reasons: ineligible patient population (n=20, 47.6%), ineligible intervention (n=14, 33.3%), ineligible study design (n=3, 7.1%), ineligible outcome measures (n=2, 4.8%), and data unavailable or nonextractable (n=3, 7.1%). The full list of excluded full-text studies, with reasons for exclusion, is provided in Multimedia Appendix 3. Ultimately, 14 studies were included in this meta-analysis (Figure 1).

These 14 studies involved a total of 794 patients diagnosed with CNSLBP. The main characteristics of the included studies, including sample size, sex distribution, interventions, and outcome measures, are summarized in Table 1. All included studies adopted an RCT design. Of these, 2 (14.3%) studies [51,52] used a 3-arm parallel-group design, whereas the remaining 12 (85.7%) studies [53-64] used a 2-arm parallel-group design. Stratified by comparator intensity, 6 (42.9%) studies [51,54,55,59,62,63] were classified as active control trials, and 8 (57.1%) studies [52,53,56-58,60,61,64] were classified as minimal or nonactive control trials.

The included trials evaluated diverse telerehabilitation models, including app-based programs, web- or video-based exercise, virtual reality, telephone-supported exercise instruction, and synchronous videoconference-based telerehabilitation. Delivery mode, contact format, exercise prescription and progression, therapist supervision, feedback mechanisms, adherence monitoring, safety or symptom exacerbation monitoring, and comparator intensity varied substantially across studies. Comparator conditions were classified as active controls or minimal or nonactive controls based on the actual treatment components, supervision intensity, and degree of individualization. Detailed intervention characteristics, rehabilitation process features, comparator classifications, and classification rationales are presented in Table 2.

Risk of bias was assessed using the Cochrane RoB 2.0 tool (Figure 2). Overall, 10 (71.4%) studies [51-56,59,61,63,64] were judged to have some concerns, 2 (14.3%) studies [57,60] were rated as being at high risk of bias, and 2 (14.3%) studies [58,62] were judged to be at low risk of bias. The main sources of bias were related to the randomization process, deviations from intended interventions, and outcome measurement. Several trials provided insufficient information on sequence generation, allocation concealment, or baseline comparability. In addition, blinding of participants and therapists was generally difficult because of the nature of telerehabilitation and exercise-based interventions. As the main outcomes were patient-reported, including pain intensity, functional disability, and kinesiophobia, participants’ awareness of group allocation may have influenced adherence, expectations, or outcome reporting. The 2 studies rated as high risk of bias were mainly affected by missing outcome data and deviations from intended interventions.

The GRADE assessment is presented in Table 3. The certainty of evidence for most outcomes was low or very low, mainly due to risk of bias, inconsistency, and imprecision. In particular, blinding of the interventions was inherently difficult, and most outcomes were based on subjective reporting, which increased the risk of bias in some studies. Furthermore, the included studies were generally limited by small sample sizes, and variations in intervention modalities, comparator intensity, and follow-up schedules across studies further lowered the certainty of the evidence.

For pain intensity, the leave-one-out analysis showed that sequential omission of individual studies did not materially change the direction or statistical significance of the pooled effect, with pooled MDs ranging from −0.88 to −1.17 (Figure S1 in Multimedia Appendix 5). After excluding a study with fewer than 20 participants in either arm [63], the pooled effect remained statistically significant (MD −0.97, 95% CI −1.76 to −0.18; Figure S2 in Multimedia Appendix 5). Similarly, after excluding a study judged as having a high risk of bias [60], the pooled effect remained statistically significant (MD −1.00, 95% CI −1.83 to −0.17; Figure S3 in Multimedia Appendix 5). These findings suggest that the pain outcome was generally robust, although substantial heterogeneity persisted across sensitivity analyses.

For functional disability, the leave-one-out analysis showed that the direction of the pooled effect remained consistent, but statistical significance was not fully stable. Sequential omission of individual studies yielded pooled MDs ranging from −5.15 to −8.41, and the 95% CI crossed the null after removal of several studies (Figure S4 in Multimedia Appendix 5). After excluding studies at high risk of bias [57,60], the pooled effect was attenuated and no longer statistically significant (MD −6.21, 95% CI −14.30 to 1.87; I²=84.2%; Figure S5 in Multimedia Appendix 5). These findings indicate limited robustness of the functional disability outcome.

For kinesiophobia, the leave-one-out analysis showed that the pooled result was sensitive to the omission of individual studies. After exclusion of a study by Karaduman and Ataş Balci [51], the pooled effect became statistically significant (MD −4.33, 95% CI −7.91 to −0.76; P=.03; Figure S6 in Multimedia Appendix 5). After excluding studies judged as having a high risk of bias [60], the pooled effect remained nonsignificant (MD −2.03, 95% CI −7.09 to 3.02; I²=84.6%; Figure S7 in Multimedia Appendix 5). These findings indicate limited robustness of the kinesiophobia outcome and suggest that this result should be interpreted cautiously.

The funnel plot for pain intensity showed some visual asymmetry, with smaller studies appearing unevenly distributed around the pooled effect estimate (Figure S8 in Multimedia Appendix 5). However, Egger’s regression test did not indicate statistically significant small-study effects (t₁₀=−2.06; P=.07).

For functional disability, the funnel plot showed slight visual asymmetry (Figure S9 in Multimedia Appendix 5), but Egger’s regression test did not indicate statistically significant small-study effects (t₈=−0.85; P=.42).

Given the substantial heterogeneity in the pooled analyses for pain intensity and functional disability (I²=90% and I²=83%, respectively), funnel plot asymmetry and Egger test results should be interpreted cautiously, as they may have been influenced by clinical and methodological heterogeneity. Overall, the current findings did not provide statistically significant evidence of small-study effects.

As only 6 (42.9%) studies were included for kinesiophobia, the Egger test was not performed for this outcome because of insufficient statistical power [50].

This systematic review and meta-analysis included 14 RCTs involving 794 adults with CNSLBP. Telerehabilitation was associated with statistically significant average reductions in pain intensity and functional disability compared with control conditions, whereas its effect on kinesiophobia was not statistically significant. However, these findings should be interpreted cautiously because the certainty of evidence was low or very low, heterogeneity was substantial across the main meta-analyses, and the 95% PIs crossed the null for all main outcomes.

The substantial heterogeneity limits confidence in the consistency and generalizability of the pooled estimates because random-effects summary estimates represent average effects across diverse clinical and intervention contexts, whereas PIs describe the expected distribution of true effects across settings [65,66]. The observed heterogeneity was likely related to differences in comparator intensity and content, delivery mode, therapist involvement, supervision level, intervention components, adherence support, and participant characteristics. As all PIs crossed the null, the magnitude and direction of effects may vary across clinical settings and intervention models. Therefore, statistical significance in the pooled mean effect should not be interpreted as evidence of consistent clinical benefit.

The exploratory subgroup findings were consistent with this interpretation. The apparent benefits of telerehabilitation were mainly observed in comparisons with minimal or nonactive controls, whereas no clear advantage was observed over active rehabilitation controls. This pattern suggests that part of the pooled effect may reflect the added value of receiving a structured rehabilitation program compared with little or no structured care, rather than a specific advantage of the remote mode of delivery over conventional active rehabilitation. Therefore, the observed effectiveness of telerehabilitation should be interpreted in relation to comparator intensity, intervention structure, supervision intensity, and clinical context.

This context-dependent pattern may help explain the inconsistent conclusions reported in previous reviews [26-29]. Earlier syntheses often pooled studies with markedly different comparator conditions, including wait-list or no-treatment controls, education or usual care, unsupervised home exercise, and structured face-to-face rehabilitation [27,29]. When such heterogeneous comparators are combined, the pooled estimate may address a mixture of different clinical questions, including whether telerehabilitation is superior to little or no structured rehabilitation and whether it provides added benefit over structured in-person rehabilitation. If pooled effects are disproportionately influenced by studies using low-intensity or minimal or nonactive controls, the apparent benefit of telerehabilitation may be overestimated. Therefore, considering comparator intensity in both the synthesis and interpretation is important for understanding the source and clinical meaning of the observed effects.

In this review, telerehabilitation showed more evident effects against minimal or nonactive controls, possibly because it provided more structured exercise guidance, feedback, and supervision than little or no intervention. In contrast, conventional face-to-face rehabilitation and other active treatments already include effective components, such as structured exercise training, therapist guidance, and supervision [13,67]. Therefore, when telerehabilitation was compared with active rehabilitation controls, no clear advantage was observed, which is broadly consistent with previous systematic reviews of digital health interventions in populations with chronic LBP [24,68]. Overall, the clinical value of telerehabilitation may lie less in replacing conventional active rehabilitation and more in supporting self-management, improving continuity of care, and extending access to rehabilitation services when face-to-face care is limited [69,70].

Telerehabilitation should be understood as a mode of rehabilitation delivery rather than a single standardized therapeutic intervention [71,72]. The included trials varied substantially in digital format, therapeutic content, therapist involvement, feedback mechanisms, and supervision intensity. Some interventions were mainly self-directed app-based or web-based programs [53,58,59], whereas others involved synchronous videoconferencing, telephone-supported instruction, virtual reality, or hybrid models combining in-person instruction with remote follow-up [51,54,57,62]. These models may differ not only in the technology used but also in treatment dose, individualization, exercise implementation and progression, adherence support, timeliness of feedback, and the extent to which therapists can monitor symptoms or correct exercise performance. As a result, trials labeled as telerehabilitation may represent quite different rehabilitation experiences for patients. These differences may have contributed to the varying subgroup effects observed for pain intensity and functional disability.

Exploratory subgroup analyses by delivery mode suggested that self-directed or asynchronous interventions showed more evident effects than therapist-supported or synchronous interventions for pain intensity and functional disability. Subgroup analyses by supervision level also suggested possible differences for pain intensity, although this pattern was not consistently observed across all outcomes. However, delivery mode, supervision level, and comparator intensity were closely interrelated. For example, self-directed or asynchronous interventions were more often compared with minimal or nonactive controls, whereas therapist-supported or synchronous interventions were more likely to be compared with active rehabilitation. Therefore, these subgroup differences may reflect the combined influence of intervention characteristics and comparator effects, rather than the independent effect of a specific delivery mode or supervision level. As delivery mode and comparator intensity were closely linked, these subgroup patterns cannot be attributed to delivery mode alone.

Clinical relevance should be interpreted by distinguishing the pooled average effect from the expected distribution of true effects across settings. As pooled MDs describe the average intervention effect across the included studies, whereas PIs describe the range in which the true effect may be expected to fall in a new clinical setting, population, or intervention model, an average effect below the prespecified MCID threshold does not necessarily mean that clinically important benefit is unlikely in all settings [48].

For pain intensity, the pooled point estimate (MD −1.02) and its 95% CI (−1.78 to −0.26) did not reach the prespecified MCID threshold of 2.0 points [73,74], indicating that the average effect was statistically significant but below the threshold for clinically important improvement. However, the lower bound of the PI (−3.61) exceeded the MCID threshold in magnitude in the direction of benefit, suggesting that clinically important pain reduction may occur in some settings. At the same time, as the PI crossed the null (−3.61 to 1.51), little or no benefit may occur in other settings.

For functional disability, the pooled point estimate (MD −7.04) did not reach the MCID threshold of 10.0 points [74]. However, the lower bound of the 95% CI (−13.43) exceeded this threshold in magnitude in the direction of benefit, indicating that the average effect remains compatible with clinically important improvement, although the CI also included average effects smaller than the MCID. In addition, the lower bound of the PI (−27.97) suggested that clinically important functional improvement may occur in some settings. Nevertheless, because the PI also crossed the null (−27.97 to 13.91), the expected effect remains heterogeneous and uncertain across settings.

For kinesiophobia, the pooled average effect was not statistically significant, and the point estimate (MD −3.14) did not reach the MCID threshold of 5.5 points [75]. The 95% PI was wide and crossed the null (−15.04 to 8.47), indicating that the expected effect may range from clinically important improvement in some settings to little or no benefit in others. Together with the very low certainty of evidence, wide uncertainty, and sensitivity to the exclusion of individual studies, these findings indicate that the evidence for the kinesiophobia remains insufficient and unstable.

In subgroup analyses, the clinical relevance of telerehabilitation appeared more evident when compared with minimal or nonactive controls. In this subgroup, the average improvement in functional disability (MD −13.38) exceeded the MCID threshold of 10.0 points [74], whereas the average improvements in pain intensity and kinesiophobia (MD −1.77 and MD −5.20, respectively) approached but did not clearly exceed their corresponding thresholds of 2.0 and 5.5 points [73-75]. In contrast, when telerehabilitation was compared with active controls, none of the 3 average subgroup effects reached the corresponding MCID threshold, and the effect estimate for functional disability favored active rehabilitation. Thus, clinically important benefits may occur in some contexts, particularly compared with minimal or nonactive management, but the clinical relevance of telerehabilitation remains uncertain when compared with structured active rehabilitation.

Evidence for kinesiophobia remains insufficient in the overall analysis. The pooled average effect was not statistically significant, the point estimate did not reach the MCID threshold, both the CI and PI were wide and crossed the null, and the result was sensitive to the exclusion of individual studies. Although these wide intervals do not exclude clinically important improvement in some settings, the overall evidence remains insufficient and unstable. This limited robustness may reflect both the small evidence base and the complexity of kinesiophobia as a psychological and behavioral outcome. Within the biopsychosocial model of chronic pain, kinesiophobia is influenced not only by pain intensity but also by pain-related beliefs, fear avoidance behaviors, emotional distress, self-efficacy, and expectations about movement [76-78]. Therefore, improvement in kinesiophobia may require interventions that directly target cognitive and behavioral mechanisms, such as pain neuroscience education, cognitive behavioral strategies, graded activity, or graded exposure [79,80]. In this review, most telerehabilitation interventions were exercise-based or multicomponent rather than purely education-focused, and relatively few interventions included explicit components targeting fear avoidance or maladaptive pain beliefs. This may partly explain why the average effects of telerehabilitation appeared more evident for pain intensity and functional disability, whereas its effect on kinesiophobia remained unstable.

Differences between education-oriented and exercise-oriented components may also have contributed to heterogeneity. Exercise-based telerehabilitation may more directly affect pain and functional disability by increasing movement exposure, strength, motor control, and activity tolerance, whereas education- or behavior-oriented components may primarily target pain beliefs, fear avoidance, self-efficacy, and self-management [13,67,80]. However, many included interventions combined exercise, education, monitoring, and feedback; few studies were clearly dominated by education-focused approaches; and intervention components and implementation details were variably or incompletely reported. Therefore, this review could not isolate the independent contribution of each component or reliably compare education-based and exercise-based telerehabilitation as distinct intervention categories.

Several limitations should be acknowledged. First, although this review was registered in PROSPERO, the registration record underwent a major protocol amendment from the initial review question to telerehabilitation for CNSLBP. Therefore, the final review question should not be interpreted as fully prospectively registered in the same way as a review whose PICOS criteria, outcomes, and synthesis plan remained unchanged from the original registration. This weakens one of the main methodological safeguards usually associated with prospective registration, namely reducing the risk of selective review question formulation, eligibility decisions, outcome selection, or analysis planning [81,82]. To mitigate this concern, we explicitly reported the amendment history; described the final PICOS criteria and analytic decisions in detail; provided the main protocol deviations, potential implications, and corrective actions in Multimedia Appendix 1; listed excluded full-text studies with reasons; and interpreted post hoc subgroup analyses as exploratory rather than confirmatory. Nevertheless, these transparency measures cannot fully remove the limitations introduced by the major protocol amendment, and this issue should be considered when assessing the credibility and robustness of the findings.

Second, the certainty, robustness, and generalizability of the findings were limited by the small number of eligible trials, small sample sizes, substantial heterogeneity, and risk of bias in the included trials. In particular, one included trial enrolled only 8 participants [63], and several outcome-specific subgroup analyses included very few studies, which may have reduced the stability of the pooled and subgroup estimates. Most included trials were judged as having some concerns or high risk of bias. As blinding of participants and therapists is difficult in telerehabilitation and exercise-based trials [83], and because pain intensity, functional disability, and kinesiophobia were all patient-reported outcomes, the pooled estimates may have been influenced by treatment expectations, differential engagement or adherence, deviations from intended interventions, and outcome assessment related to awareness of group allocation [84].

Third, the subgroup analyses were exploratory. Comparator intensity, delivery mode, and supervision level were not mutually independent, and several subgroups included only a small number of studies. Formal meta-regression was not conducted because the number of eligible trials and outcome-specific comparisons was limited, which would make such analyses underpowered and potentially unstable [66]. Therefore, potential sources of heterogeneity could not be formally tested, and the subgroup analyses should be considered hypothesis-generating rather than confirmatory evidence that one telerehabilitation model is superior to another.

Finally, because the primary analyses preferentially pooled postintervention data, the long-term effects of telerehabilitation remain uncertain. This is particularly important for CNSLBP, which is often recurrent and requires sustained self-management rather than short-term symptom relief alone [12,85]. In addition, key implementation-related outcomes, including adherence, intervention fidelity, adverse events, safety monitoring, and economic outcomes, were inconsistently or sparsely reported across trials. These reporting gaps are important because the effectiveness, feasibility, and safety of telerehabilitation may depend on whether the intervention is delivered and used as intended [86]. Therefore, the available evidence remains insufficient to draw firm conclusions about long-term clinical effectiveness, implementation quality, and safety in routine care.

Despite these limitations, the findings have implications for rehabilitation delivery and health service planning. Telerehabilitation should not be interpreted as a universally superior replacement for structured active rehabilitation, but rather as a flexible delivery option or adjunctive strategy to support self-management, improve continuity of care, and extend access to rehabilitation services [71]. Telerehabilitation may therefore be useful for maintaining rehabilitation support between visits or after the initial assessment, including structured home exercise guidance, educational reinforcement, adherence feedback, and symptom self-monitoring when regular face-to-face rehabilitation is difficult to sustain [87,88]. Such an approach may be particularly relevant for patients living in remote areas, patients who have difficulty attending regular rehabilitation sessions, and health care settings with limited rehabilitation resources [87,89,90].

The economic value of telerehabilitation remains uncertain. Previous systematic reviews of musculoskeletal conditions have suggested that telerehabilitation may be associated with lower per-patient costs in some economic evaluations [23], and one included trial in this review also reported lower intervention costs for telerehabilitation than for outpatient rehabilitation [55]. These potential savings may be related to reduced travel, fewer facility-based visits, and lower time-related burdens for patients [91,92]. However, because economic outcomes were rarely reported and cost-related evidence varied across health care contexts [91], these findings should be interpreted cautiously.

For patients with prominent kinesiophobia or other psychological and behavioral barriers, remote exercise training alone may be insufficient because improvement in these outcomes may require interventions that directly address fear avoidance, maladaptive pain beliefs, self-efficacy, and engagement with activity [93,94]. Future telerehabilitation programs for CNSLBP should clarify whether educational content is used merely as supportive information or as an active therapeutic component. When fear avoidance is a major treatment target, programs may need to integrate psychologically informed strategies, such as pain neuroscience education, cognitive behavioral strategies, graded activity, or graded exposure [95].

Future trials should improve the reporting of treatment adherence and intervention fidelity. Across the included trials, adherence was assessed inconsistently using different indicators, such as session completion, digital engagement, logbook records, telephone follow-up, or platform-recorded activity [52-54,58,60]. Few trials clearly reported the actual exercise dose completed, intensity progression, therapist feedback, protocol deviations, or whether the intervention was delivered as intended. More standardized reporting of adherence and fidelity would help clarify whether observed effects reflect the telerehabilitation model itself or differences in actual treatment exposure and intervention implementation [86,96].

Finally, the applicability of the current evidence should be considered in light of the rapid development of digital rehabilitation technologies. Most included trials evaluated relatively simple telerehabilitation models, such as app-based exercise, video programs, telephone follow-up, virtual reality, or videoconference-based supervision. As digital rehabilitation increasingly incorporates wearable sensors, automated movement assessment, adaptive feedback, AI-supported monitoring, and hybrid remote–in-person care pathways [25,97], the current evidence may not fully represent the effectiveness, safety, adherence, or implementation feasibility of future digitally enhanced telerehabilitation models. Future trials should therefore evaluate not only clinical outcomes but also usability, engagement, safety monitoring, implementation feasibility, intervention fidelity, and cost-effectiveness, which may provide more systematic evidence for optimizing telerehabilitation delivery in contemporary digital care settings [98].

The current evidence suggests that telerehabilitation may provide context-dependent benefits for adults with CNSLBP, particularly for improving pain intensity and functional disability when compared with minimal or nonactive controls. Although the pooled average effects for pain intensity and functional disability were below the prespecified MCID thresholds, the PIs suggested that clinically important benefits may occur in some settings, whereas little or no benefit may occur in others. No clear advantage was observed over active rehabilitation controls, and evidence for kinesiophobia remains insufficient and unstable. Given the substantial heterogeneity, PIs crossing the null, risk of bias, imprecision, and low or very low certainty of evidence, these findings should be interpreted cautiously. Telerehabilitation may be considered a flexible delivery option or adjunctive strategy to support self-management and improve access to rehabilitation services, especially when face-to-face care is limited. Future high-quality RCTs are needed to clarify which telerehabilitation models are effective, for whom, and under what clinical conditions.