Types of studies

We will include randomised controlled trials (RCTs) with clearly reported true randomisation methods, cross‐over RCTs and cluster‐RCTs. We will include studies reported as full text, those published as abstract only and unpublished data. There will be no restriction on date or language of publication.

Types of participants

We will consider trials of adult participants (aged 18 years or greater) of any sex, with non‐specific LBP that is either acute/subacute (acute being less than six weeks' duration, and subacute being six to 12 weeks' duration) or chronic (greater than 12 weeks' duration). Non‐specific LBP will be defined as pain not attributed to a recognisable or specific pathology, such as radicular syndromes or serious pathology (i.e. fracture, cancer, infection and inflammatory diseases). We will exclude studies that included individuals with specific conditions such as LBP related to pregnancy, infection, fracture, spinal stenosis, cancer, and individuals with pain less than six months after spinal surgery. Studies including a mixed population (e.g. musculoskeletal pain) will be excluded, unless separate data were provided for LBP patients. We will contact study authors if information about the population with LBP is not provided separately. No restriction will be placed on the setting or context of the studies.

Types of interventions

We will consider any health intervention delivered remotely through telecommunication networks or the internet, including telephone calls, short message service (SMS), website, videoconferencing systems, software and mobile application (app). Telerehabilitation will be classified into three main categories according to the most predominant component of the intervention:

• education or psychological interventions (behavioural and psychotherapeutic treatments designed to reduce psychological distress and maladaptive behavior, e.g. cognitive behavioural therapy (CBT), counselling);

• exercise and physical activity (this includes general or specific exercises and strategies to increase physical activity levels);

• others, including multi‐component interventions (when the telerehabilitation intervention includes both a psychological component and an exercise or physical activity component).

We will consider mixed interventions (i.e. a combination of face‐to‐face and telerehabilitation components) if the telerehabilitation component comprises at least 75% of either the planned sessions or the time of the intervention.

Telerehabilitation will be compared to usual care, minimal interventions (e.g. no treatment, waiting list, advice), and a similar face‐to‐face intervention (e.g. exercise). The main comparison reported in the 'Summary of findings' table(s) will be telerehabilitation versus usual care.

Types of outcome measures

Electronic searches

We will perform computerised electronic searches of the following databases, from inception to the present.

• Cochrane Central Register of Controlled Trials (CENTRAL) (the Cochrane Library, current issue, which includes the Cochrane Back and Neck trials register)

• MEDLINE via OvidSP (1946 to current)

• Embase via OvidSP (1980 to current)

• Cumulative Index to Nursing and Allied Health Literature (CINAHL, EBSCO) (1982 to current)

• Physiotherapy Evidence Database (PEDro)

• ClinicalTrials.gov

• WHO International Clinical Trial Registry Platform (WHO ICTRP)

Search strategies will be developed using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019a). The search strategy for MEDLINE can be found in Appendix 1. It will be translated as closely as possible across the other databases. We will not apply any restrictions on date, language or publication status to the searches.

Searching other resources

We will check the reference lists of all primary studies and previous systematic reviews on this topic to identify additional studies. We will search for errata or retractions from included studies published in full text on PubMed, and report the date this was done.

Selection of studies

After merging search results and discarding duplicates, two review authors (LA and BS) will independently screen titles and abstracts of all reports identified as a result of the search. We will retrieve the full text of potentially relevant reports and two authors (LA and BS) will independently screen the full text and identify studies for inclusion. They will also identify and record reasons for excluding ineligible studies. We will resolve any disagreements between the review authors through discussion, or by arbitration by a third person (LC or SK) when consensus cannot be reached. We will identify and exclude duplicates ad collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review. We will report the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table (PRISMA Group 2009).

Data extraction and management

We will use a data collection form for study characteristics and outcome data, which we will pilot on at least one study in the review. Two review authors (LA and BS) will independently extract relevant data from each of the included studies. We will extract the following study characteristics.

• Bibliometric data (e.g. authors, year, and language)

• Methods (e.g. study design, duration of study, sample size, country, withdrawals, clinical trial registration and funding)

• Participants (e.g. number, gender, mean age, age range, symptoms, inclusion and exclusion criteria and severity of the condition)

• Interventions: intervention (including the type of technology used e.g. telephone, app, and/or website), comparison, concomitant medications, and co‐interventions. We will collect the reporting of interventions according to the Template for Intervention Description and Replication (TIDieR) checklist (Hoffmann 2014; Yamato 2016) (Appendix 2)

• Outcomes: primary and secondary outcomes specified and collected, and time points reported

• Characteristics of the design of the trial, as outlined below in Assessment of risk of bias in included studies

• Notes: funding for the trial and notable declarations of interest of trial authors

• Whether the trial was prospectively registered or not

We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way and when data were transformed or estimated from graph. We will use PlotDigitizer software (PlotDigitizer [Computer program]) to extract data from graphs or figures (we will extract these data in duplicate). We will resolve disagreements by consensus or by involving a third person (LC or CM). One review author (LA) will transfer data into the Review Manager 5 file (Review Mannager 2014). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports.

We will select data based on the following decision rules.

• We will give preference to change scores if both change and endpoint values are available.

• We will give preference to intention‐to‐treat (ITT) analysis data rather than 'per protocol' or 'as treated', if available.

• If multiple time points are reported, we will use the one closest to three months for short‐term follow‐up, and six months for intermediate‐term follow‐up. We will collect all available long‐term follow‐up data.

Where additional data about treatment effects, as well as other characteristics, are required, we will contact study authors up to three times. If no reply is received within six weeks, we will consider the data unobtainable for this iteration of the review. Where there are discrepancies between published and unpublished versions of the same data, we will give preference to the published data because these have been through a peer review process.

Assessment of risk of bias in included studies

The assessment of risk of bias in included studies will be performed using the methods outlined in the Handbook (Higgins 2019a). This will be done independently by two review authors (LA and BS) disagreements will be resolved by discussion or arbitration by a third author (LC or SK). We will assess the risk of bias using the Cochrane risk of bias assessment tool from the Back and Neck Group (Furlan 2015) (Table 1; Table 2). We will assess each of the 13 items of the 'Risk of bias' assessment tool as being at high, low or unclear risk of bias. We will provide a quote from the study report, together with a justification for our judgement, in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgment across different studies for each of the domains listed. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table. When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome. We will present the figures generated by the 'Risk of bias' tool to provide summary assessment of the risk of bias.

We will conduct the review according to this published protocol and report any deviations from it in the 'Differences between protocol and review' section of the systematic review.

Assessment of bias in conducting the systematic review

We will conduct the review according to this published protocol and report any deviations from it in the 'Differences between protocol and review' section of the systematic review

Measures of treatment effect

We will analyse the primary outcomes (i.e. pain intensity and disability) and present these on a continuous scale (ranging from zero to 100) as mean differences (MDs) with 95% confidence intervals (CIs). For the secondary outcomes presented as continuous measures (e.g. health‐related quality of life), we will express pooled effects with standardised mean difference (SMD) and 95% CIs if these trials used different measurement scales to assess these outcomes. If the studies presented the same outcome measures, we will use mean difference. Dichotomous outcomes (e.g. adverse events, return to work) will be expressed as risk differences and 95% CIs. To facilitate interpretation, we will translate pooled SMD values to the equivalent in commonly used scales for measuring disability, using the standard deviation reported in the included studies.

For dichotomous outcomes, we will calculate the number needed to treat for an additional beneficial outcome (NNTB), or number needed to treat for an additional harmful outcome (NNTH) from the control group event rate and the relative risk using the Visual Rx NNT calculator (Cates 2008). We will calculate the NNTB for continuous measures using the Wells calculator (available at the Cochrane Musculoskeletal website, musculoskeletal.cochrane.org). We will only calculate NNTB or NNTH for outcomes showing a statistically significant benefit or harm.

For dichotomous outcomes, we will calculate the absolute change from the difference in the risk between the intervention and control group using GRADEpro GDT, and express this as a percentage (GRADEpro GDT 2015). We will calculate the relative change as the risk ratio minus one, and will express this as a percentage. For continuous outcomes, we will calculate the absolute change by dividing the mean difference by the scale of the measure and expressing it as a percentage. We will calculate the relative difference as the absolute benefit (mean difference) divided by the baseline mean of the control group, and express this as a percentage.

In the 'Comments' column of the 'Summary of findings' table, we will report the absolute percentage difference and the relative percentage change from baseline. For outcomes that show a significant difference between treatment groups, we will also report the NNTB or NNTH.

Unit of analysis issues

The unit of analysis will be the participant for all trials. Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting (e.g. two groups of different interventions and one waiting‐list control). If we identify any cross‐over trials, we will only extract data from the first phase of the trial to avoid potential carry‐over effects. If we identify any cluster‐RCTs or studies that included more than one joint in the analysis, we will multiply the standard error of the effect estimate (from an analysis ignoring clustering) by the square root of the design effect (inflated variances), according to the methods described in Chapter 23 of the Handbook (Higgins 2019b). The meta‐analysis using the inflated variances will be performed using the generic inverse‐variance method.

Dealing with missing data

We will contact trial authors or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data when possible (e.g. when a study is identified as abstract only or when data are not available for all participants). When this is not possible and the missing data are likely to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis. We will clearly describe any assumptions and imputations to handle missing data and explore the effect of imputation by sensitivity analyses.

For dichotomous outcomes (e.g. number of withdrawals due to adverse events), we will calculate the withdrawal rate using the number of participants randomised in the group as the denominator. For continuous outcomes (e.g. mean change in pain intensity score), we will calculate the MD or SMD, based on the number of participants analysed at that time point. If the number of participants analysed is not presented for each time point, we will use the number of the randomised patients in each group at baseline.

When possible, we will compute missing standard deviations (SDs) from other statistics such as standard errors (SEs), CIs or P values, according to the methods recommended in the Handbook (Higgins 2019a). If SDs cannot be calculated, we will impute them (e.g. from other studies in the meta‐analysis).

Assessment of heterogeneity

We will assess clinical and methodological diversity in terms of participants, interventions, outcomes and study characteristics for the included studies to determine whether a meta‐analysis is appropriate. We will do this by examining these data from the data extraction tables. We will assess statistical heterogeneity by visual inspection of the forest plot to assess for obvious differences in results between the studies. We will also use the I² and Chi² statistical tests.

As recommended in the Handbook (Deeks 2019), we will interpret I² values as follows.

• 0% to 40%: might not be important

• 30% to 60%: may represent moderate heterogeneity

• 50% to 90%: may represent substantial heterogeneity

• 75% to 100%: considerable heterogeneity

As noted in the Handbook, the importance of I² depends on the magnitude and direction of effects, and strength of evidence for heterogeneity. The Chi² test will be interpreted where a P value of 0.10 or less indicates evidence of statistical heterogeneity.

We will create and examine a funnel plot to explore possible small‐study biases. When interpreting funnel plots, we will examine the different possible reasons for asymmetry, and relate this to the results of the review. If we are able to pool more than 10 trials, we will undertake formal statistical tests to investigate funnel plot asymmetry, and will follow the recommendations in Chapter 10 of the Handbook (Sterne 2017).

To assess outcome reporting bias, we will check trial protocols against published reports. For studies published after 1 July 2005, we will screen the Clinical Trial Register at the International Clinical Trials Registry Platform of the World Health Organization (www.who.int/ictrp/en) for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

We will use a random‐effects model for all meta‐analyses only where meta‐analysis is meaningful; that is, if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense. We will use alternative synthesis methods, such as summary of effect estimates (e.g. median, interquartile range with box plots) or the combination of P values in the circumstance where there is no, or minimal, information reported on the direction of effect (McKenzie 2019).

Assessment of reporting biases

We will create and examine a funnel plot to explore possible small‐study biases. When interpreting funnel plots, we will examine the different possible reasons for asymmetry, and relate this to the results of the review. If we are able to pool more than 10 trials, we will undertake formal statistical tests to investigate funnel plot asymmetry, and will follow the recommendations in Chapter 10 of the Handbook (Sterne 2017).

To assess outcome reporting bias, we will check trial protocols against published reports. For studies published after 1 July 2005, we will screen the Clinical Trial Register at the International Clinical Trials Registry Platform of the World Health Organization (www.who.int/ictrp/en) for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

Data synthesis

We will use a random‐effects model for all meta‐analyses only where meta‐analysis is meaningful; that is, if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense. We will use alternative synthesis methods, such as summary of effect estimates (e.g. median, interquartile range with 'box‐and‐whisker' plots) or the combination of P values in the circumstance where there is no, or minimal, information reported on the direction of effect (McKenzie 2019).

Subgroup analysis and investigation of heterogeneity

We will stratify the analyses based upon the duration of follow‐up reported for each outcome (that is, short‐, intermediate‐, and long‐term); and also based upon duration of symptoms (acute/subacute and chronic). We will also perform a subgroup analysis for telerehabilitation modality (phone, website, app, video conference). We will use the formal test for subgroup interactions in Review Manager 5 (Review Mannager 2014).

Sensitivity analysis

We plan to carry out the following sensitivity analyses for the main comparison to investigate the robustness of the treatment effect for pain intensity and physical function (all time points).

• Studies we judge as being at low risk of selection bias (i.e. we will exclude all studies with unclear or high risk of selection bias);

• Studies we judge as being at low risk of detection bias (i.e. we will exclude all studies with unclear or high risk of detection bias);

• Studies we judge as being at low risk of attrition bias (i.e. we will exclude all studies with unclear or high risk of attrition bias).

If studies are rated as being at high risk of bias for at least one of these bias domains, we will consider the overall risk of bias for the study as high. We will follow the same decision for data synthesis and unit of analysis issues as in the main analyses.

Interpreting results and reaching conclusions

We will follow the guidelines for interpreting results in Chapter 12 of the Handbook (Schünemann 2019b), and will be aware of distinguishing a lack of evidence of effect from a lack of effect. We will base our conclusions only on findings from the quantitative or narrative synthesis of included studies for this review. We will avoid making recommendations for practice, and our implications for research will suggest priorities for future research and outline what the remaining uncertainties are in the area.