Telerehabilitation for neck pain

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To evaluate the effectiveness of telerehabilitation to improve pain and function compared to no treatment, waiting list, usual care, or any other active intervention in people with acute, subacute and chronic neck pain.

Background

Description of the condition

Neck pain is a very common condition and is associated with disability worldwide (Carroll 2009; Hogg‐Johnson 2008). Neck pain is the fourth most burdensome condition in terms of years lived with disability (Hoy 2010; Hurwitz 2018; Vos 2016), with a one‐year prevalence of 20.3% (Genebra 2017; Hoy 2010), and lifetime prevalence of 27% to 71% (Chiu 2006; Côté 1998; Lau 1996; Mäkelä 1991). In the coming decades, it is expected that the number of people with neck pain will increase due to ageing populations and child survival (Vos 2016). A peak prevalence is observed in middle age groups at 35 to 49 years (Bot 2005; Hogg‐Johnson 2008; Rekola 1993). It is estimated that approximately 43% of people with neck pain will be fully recovered from their symptoms in one year (Vasseljen 2013). However, residual pain and recurrences are often observed, in 50% to 85% of people in one to five years (Carroll 2009; Cohen 2015).

Neck pain is defined by its location, which starts at the superior nuchal line and continues down to the level of scapula and shoulder (Bier 2018; Guzman 2009). Non‐specific neck pain comprises the largest group of people with neck pain, and it is defined as pain not attributed to a recognisable or specific pathology (e.g. nerve root compromise, fracture, cancer or inflammatory diseases) or when there are no features (i.e. red flags) to suggest more serious conditions (Bier 2018; Guzman 2009). Neck pain can also arise from clinical manifestations and signs and symptoms as a consequence of a trauma or traffic collision (whiplash‐associated disorders) (Blanpied 2017; Guzman 2009; Spitzer 1995). Other common neck disorders include cervicogenic headache and neck pain with radiating pain (radiculopathy) (Blanpied 2017; Bogduk 2004; Bono 2011; Falco 2012;). Neck pain is also classified according to the duration of symptoms as acute (less than 6 weeks), subacute (6 to 12 weeks) and chronic (more than 12 weeks) (Blanpied 2017; Cohen 2015).

Description of the intervention

There are a wide range of interventions available for people with neck pain. The most recent clinical practice guidelines recommend exercise, manual therapy, advice and education for people with neck pain (Bier 2018; Blanpied 2017; Monticone 2016; Morley 2011). Remotely delivered interventions, including telerehabilitation, have the potential to increase access to general healthcare services, deliver care to rural areas, offer providers greater flexibility in scheduling, and save people's time and resources in seeking care (Kruse 2018).

Remotely delivered interventions can be defined as the use of information and communication technologies to provide health services and rehabilitation at a distance (Finkelstein 2000; Scalvini 2004). Telerehabilitation can be broadly defined as the delivery of rehabilitation services over telecommunication technologies such as websites, smartphone apps, videoconferencing systems and telephone (Russell 2007). Telerehabilitation can be considered a subfield of telehealth (Russell 2007). Telerehabilitation can provide a platform to deliver services offered by a number of health disciplines including physiotherapy, occupational therapy, dietetics, psychology and others. Further, telerehabilitation may involve the full spectrum of client care including the client interview, physical assessment and diagnosis, treatment, maintenance activities, consultation, education and training. Healthcare providers have developed telerehabilitation services to increase access to health care, especially for rural populations, people with a disability, or people living in highly‐populated cities where healthcare systems can be overcrowded. Telerehabilitation overcomes some of the potential barriers to healthcare access such as travel (distance, traffic, transport), time consumed, high demand for the public health system (long waiting lists), lack of insurance cover for private care, and high costs for long‐term treatment (Kairy 2009; Lee 2018). Telerehabilitation interventions can include any type of treatment ‐ such as treatment based on education, exercise prescription and self management ‐ that can be offered at a distance (Gialanella 2017; Scalvini 2004). The most common ways to deliver telerehabilitation interventions are through websites, smartphone apps, videoconferences, over the telephone and text messages.

Telerehabilitation interventions have been growing in popularity in recent years with advances in technologies and telecommunication (Cottrell 2020). People may choose telerehabilitation interventions to avoid long waiting lists, reduce costs, because of a lack of transport or for other reasons (Cottrell 2020; Kairy 2009; Lee 2018). Around one‐fifth of people with neck pain living in rural areas seek primary health care (Holmberg 2006), but they generally face difficulties in accessing health care due to long distances and waiting lists (Cottrell 2020; Gardner 2016; Hogg‐Johnson 2008). Thus, it is possible that these people could benefit from telerehabilitation interventions.

How the intervention might work

Telerehabilitation interventions are a mode of healthcare delivery. Therefore, the mechanisms that lead to improvement of symptoms, in theory, should be similar to those observed in a face‐to‐face rehabilitation model (Laver 2013). Telerehabilitation can be delivered in a synchronous mode, in which a clinician or healthcare centre provides real‐time patient care (online), or asynchronous mode (store‐and‐forward or offline) with electronic transmission of medical information, such as images, documents and prerecorded videos (Scalvini 2004). These interventions can be tailored to people's needs (e.g. exercise via teleconference) or included in a generic program.

Why it is important to do this review

The use of telerehabilitation in the treatment of people with neck pain can be useful for a large number of people with limited access to health services (Gialanella 2017; Jay 2014). Moreover, telerehabilitation can overcome common barriers to health care access such as lack of time, issues with transport and costs for treatment (Cottrell 2020; Doorenbos 2011; Gardner 2016; Kairy 2009; Scalvini 2004; Theodoros 2008). Finally, telerehabilitation has been used in a wide range of fields, including paediatrics (Tan 2012), pneumology (McLean 2010), musculoskeletal pain (Dario 2017), and neurology (Khan 2015; Laver 2013). Several studies have investigated the benefits of telerehabilitation for people with neck pain (Blodt 2014; Gialanella 2017; Huis 2010; Hutting 2015; Jay 2014; Lee 2017). To date, the effect of telerehabilitation on neck pain remains uncertain because there is no systematic review summarising the current evidence to help individuals, clinicians and stakeholders to support their healthcare decisions. Therefore, a high quality systematic review is needed to investigate the effectiveness of telerehabilitation for people with neck pain.

Objectives

To evaluate the effectiveness of telerehabilitation to improve pain and function compared to no treatment, waiting list, usual care, or any other active intervention in people with acute, subacute and chronic neck pain.

Methods

Criteria for considering studies for this review

Types of studies

We will only include randomised trials (including cross‐over or parallel group and individually or cluster‐randomised trials). We will include studies reported as full text, those published as abstract only, and unpublished data. We will not include trials with quasi‐random allocation procedures (such as alternation, hospital record numbers, dates of birth, etc.). There will be no restriction on date or language of publication.

Types of participants

We will include trials in adult participants with acute, subacute or chronic neck pain. We will include neck pain categorised as follows.

• Non‐specific neck pain defined as pain not attributed to a recognisable or specific pathology (Bier 2018; Guzman 2009).

• Neck disorders associated with radiculopathy (Klippel 2008; Rubinstein 2007).

• Neck pain associated with whiplash‐associated disorder (WAD) grades I, II and III (Guzman 2009; Spitzer 1995), degenerative changes and myofascial pain syndrome (Klippel 2008).

We will include trials studying multiple pain conditions if separate data for neck pain are available. We will exclude trials which enrolled participants post‐surgery (in the previous six months) or with specific conditions such as fracture, spinal stenosis, inflammatory diseases, cancer, cervicogenic headache, causes of headache not of cervical origin but associated with the neck, coexisting headache not provoked by movements or sustained neck postures, or 'mixed' subtypes of headache (e.g. migraine and cervicogenic headache) and WAD grade IV (Guzman 2009; Spitzer 1995).

Types of interventions

We will include all types of telerehabilitation; that is, any intervention delivered over telecommunication networks or Internet, including websites, videoconferencing systems, software, smartphone apps and telephone. We will classify telerehabilitation into three main categories according to the predominant component of the intervention:

• psychological interventions (behavioral and psychotherapeutic treatments designed to reduce psychological distress and maladaptive behavior, such as cognitive behavioural therapy (CBT) or counselling), or educational interventions;

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

• others, including multi‐component interventions where psychological interventions and exercise are both key interventions.

We will include hybrid interventions (i.e. face‐to‐face and remotely delivered) if at least 75% of the total intervention treatment was delivered remotely.

Types of outcome measures

Primary outcomes

• Pain intensity as a continuous outcome (in the following order of preference: Numerical Rating Scale (NRS), Visual Analogue Scale (VAS), McGill Pain Questionnaire, other validated scale). For trials reporting pain as a dichotomous outcome (e.g. 30% or 50% reduction in pain intensity), we will include those data as a secondary outcome.

• Function as a continuous outcome (in the following order of preference: Neck Disability Index (NDI), Pain Disability Index (PDI), Functional Rating Index (FRI), other validated scale). For trials reporting function as a dichotomous outcome, we will include those data as a secondary outcome.

• Health‐related quality of life as a continuous outcome (in the following order of preference: 12‐Item Short Form health survey (SF‐12), EQ‐5D, physical and mental health domains of 36‐Item Short Form Health Survey questionnaire (SF‐36), other algofunctional scale).

• Anxiety as a continuous outcome (in the following order of preference: Hospital Anxiety and Depression Scale; the Spielberger State‐Trait Anxiety Inventory; other validated scale).

• Depression as a continuous outcome (in the following order of preference: Hospital Anxiety and Depression Scale; Centre for Epidemiological Studies Depression Scale; Beck Depression Inventory; other validated scale).

• Any adverse events as dichotomous outcomes (e.g. fatigue, soreness, stiffness and worsening of pain).

• Withdrawals due to adverse events (as dichotomous outcomes).

• Short‐term serious adverse events from trials as dichotomous outcomes (e.g. cardiovascular events).

Secondary outcomes

• Return to work as a dichotomous outcome (e.g. percentage of people who returned to work after neck pain).

• Self‐efficacy as a continuous outcome (in the following order of preference: Pain Self‐Efficacy Questionnaire; Chronic Pain Self‐Efficacy Scale; other validated scale).

• Fear avoidance as a continuous outcome (in the following order of preference: Fear‐Avoidance Belief Questionnaire; other validated scale).

• Pain catastrophisation as a continuous outcome (in the following order of preference: Pain Catastrophising Scale; other validated scale).

• Intervention adherence as a dichotomous outcome (expressed in percentages or number of participants).

We will consider three follow‐up time points: short‐term (≤ 3 months after randomisation), medium‐term (> 3 months to < 12 months after randomisation), and long‐term (≥ 12 months after randomisation). If there are multiple follow‐up time points classified within the same category, we will use the one that is closest to three months for the short‐term time point, closest to six months for the medium‐term time point, and longer than six months and closest to 12 months for the long‐term follow‐up time point.

Search methods for identification of studies

Electronic searches

We will perform computerised electronic searches on the following databases.

• Cochrane Central Register of Controlled Trials (CENTRAL, current issue) in the Cochrane Library.

• MEDLINE Ovid (1946 to current).

• Embase Ovid (1980 to current).

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

• AMED Ovid (Allied and Complementary Medicine; 1985 to current).

• PEDro (Physiotherapy Evidence Database; 1999 to current).

• African Index Medicus (AIM; 1982 to current).

• LILACS (Latin American and Caribbean Health Science Information database; 1982 to current).

We will use the search strategies recommended by the Cochrane Back and Neck Review Group (Furlan 2015). The complete search strategy for MEDLINE is available in Appendix 1.

Searching other resources

We plan to identify relevant unpublished and ongoing clinical trials. We will extend the search to the WHO International Clinical Trial Registry Platform (WHO ICTRP; www.who.int/ictrp/en/) and ClinicalTrials.gov. We will check the reference list of eligible studies and previous systematic reviews on this topic to identify additional studies.

Data collection and analysis

Selection of studies

One review author (JF) will conduct the electronic searches. Two review authors (JF and BS) will independently perform the exclusion of duplicates, followed by screening titles, abstracts and full‐text versions of all potentially eligible records identified by the electronic searches. We will resolve any disagreements between the review authors through discussion or by arbitration of a third review author (LC). We will record our screening process using a PRISMA flow chart (Liberati 2009). We will present studies excluded at the full‐text stage and give reasons for their exclusion in this flow chart. Studies will not be excluded on basis of outcome reporting.

Data extraction and management

We will extract relevant data from each of the eligible studies using a standardised data extraction form. Two review authors (JF and BS) will independently extract all data. We will resolve disagreements by discussion or by referral to a third review author (LC) as necessary. We will extract the following information about included studies.

• Bibliometric data (authors, year, language).

• Study characteristics (design, sample size, country, funding).

• Characteristics of the participants (gender, age, symptoms, severity of the condition).

• Description of the interventions (adherence, number of sessions, duration of sessions, co‐interventions).

• Duration of follow‐up assessments, outcomes assessed, study results, and time periods for outcome assessment (short‐, medium‐ and long‐term).

• Sources of funding: financial conflicts of interest and declarations of interest of trial authors.

• Notes: trial registration (prospectively or retrospectively registered).

We plan to extract and assess the completeness of the description of the interventions using the TIDieR checklist (Hoffmann 2014; Yamato 2018) (Appendix 2). Where multi‐arm studies also include interventions that are not of interest to this review, we will include these studies and extract only the data for the comparisons between interventions of interest.

We will extract data based on the following decision rules.

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

• 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, six months for medium‐term, and longer than six months and closest to 12 months for long‐term follow‐ups.

Where additional data about treatment effects as well as other characteristics are required, we will contact study authors up to three times. If we receive no reply 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.

Main planned comparisons

Our primary comparison will be telerehabilitation versus usual care or no treatment.

Our other comparisons are grouped as follows.

• Telerehabilitation versus other treatments.

• Telerehabilitation plus other treatment versus other treatment alone.

Assessment of risk of bias in included studies

We will perform assessment of risk of bias in included studies using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (hereafter referred to as the Cochrane Handbook,Higgins 2017), and the Cochrane risk of bias assessment tool from the Back and Neck Group (Furlan 2015). Two review authors (JF and BS) will independently perform risk of bias assessment and will resolve disagreements through discussion, or arbitration by a third reviewer (LC) if necessary. Each of the 13 items of the risk of bias assessment will be scored as 'high', 'low' or 'unclear' risk of bias (Table 1; Table 2). We will provide a quote from the study report, together with a justification for our judgement, in the 'Risk of bias' tables. We will summarise the risk of bias judgements 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' tables. 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 a summary assessment of the risk of bias.

1. Sources of risk of bias.

Bias domain	Source of bias	Possible answers
Selection	(1) Was the method of randomisation adequate?	Yes/no/unsure
Selection	(2) Was the treatment allocation concealed?	Yes/no/unsure
Performance	(3) Was the patient blinded to the intervention?	Yes/no/unsure
Performance	(4) Was the care provider blinded to the intervention?	Yes/no/unsure
Detection	(5) Was the outcome assessor blinded to the intervention?	Yes/no/unsure
Attrition	(6) Was the drop‐out rate described and acceptable?	Yes/no/unsure
Attrition	(7) Were all randomised participants analysed in the group to which they were allocated?	Yes/no/unsure
Reporting	(8) Are reports of the study free of suggestion of selective outcome reporting?	Yes/no/unsure
Selection	(9) Were the groups similar at baseline regarding the most important prognostic indicators?	Yes/no/unsure
Performance	(10) Were co‐interventions avoided or similar?	Yes/no/unsure
Performance	(11) Was the compliance acceptable in all groups?	Yes/no/unsure
Detection	(12) Was the timing of the outcome assessment similar in all groups?	Yes/no/unsure
Other	(13) Are other sources of potential bias unlikely?	Yes/no/unsure

Furlan 2015

2. Criteria for a judgment of 'yes' for the sources of risk of bias.

1	A random (unpredictable) assignment sequence. Examples of adequate methods are coin toss (for studies with 2 groups), rolling a die (for studies with 2 or more groups), drawing of balls of different colours, drawing of ballots with the study group labels from a dark bag, computer‐generated random sequence, preordered sealed envelopes, sequentially‐ordered vials, telephone call to a central office, and preordered list of treatment assignments. Examples of inadequate methods are: alternation, birth date, social insurance/security number, date in which they are invited to participate in the study, and hospital registration number.
2	Assignment generated by an independent person not responsible for determining the eligibility of the participants. This person has no information about the persons included in the trial and has no influence on the assignment sequence or on the decision about eligibility of the participant.
3	Index and control groups are indistinguishable for the participants, or if the success of blinding was tested among the participants and it was successful.
4	Index and control groups are indistinguishable for the care providers, or if the success of blinding was tested among the care providers and it was successful.
5	Adequacy of blinding should be assessed for each primary outcome separately. This item should be scored 'yes' if the success of blinding was tested among the outcome assessors and it was successful, or: ‐for participant‐reported outcomes in which the participant is the outcome assessor (e.g. pain, disability): the blinding procedure is adequate for outcome assessors if participant blinding is scored ‘yes’ ‐for outcome criteria assessed during scheduled visit and that supposes a contact between participants and outcome assessors (e.g. clinical examination): the blinding procedure is adequate if participants are blinded, and the treatment or adverse effects of the treatment cannot be noticed during clinical examination ‐for outcome criteria that do not suppose a contact with participants (e.g. radiography, magnetic resonance imaging): the blinding procedure is adequate if the treatment or adverse effects of the treatment cannot be noticed when assessing the main outcome ‐for outcome criteria that are clinical or therapeutic events that will be determined by the interaction between participants and care providers (e.g. co‐interventions, hospitalisation length, treatment failure), in which the care provider is the outcome assessor: the blinding procedure is adequate for outcome assessors if item ‘4’ (caregivers) is scored ‘yes’ ‐for outcome criteria that are assessed from data of the medical forms: the blinding procedure is adequate if the treatment or adverse effects of the treatment cannot be noticed on the extracted data
6	The number of participants who were included in the study but did not complete the observation period or were not included in the analysis must be described and reasons given. If the percentage of withdrawals and drop‐outs does not exceed 20% for short‐term follow‐up and 30% for long‐term follow‐up and does not lead to substantial bias, a ‘yes’ is scored. (N.B. these percentages are arbitrary, not supported by literature).
7	All randomised participants are reported/analysed in the group they were allocated to by randomisation for the most important moments of effect measurement (minus missing values) irrespective of noncompliance and co‐interventions.
8	All the results from all prespecified outcomes have been adequately reported in the published report of the trial. This information is either obtained by comparing the protocol and the report, or in the absence of the protocol, assessing that the published report includes enough information to make this judgment.
9	Groups have to be similar at baseline regarding demographic factors, duration and severity of complaints, percentage of participants with neurological symptoms, and value of main outcome measure(s).
10	If there were no co‐interventions or they were similar between the index and control groups.
11	The reviewer determines if the compliance with the interventions is acceptable, based on the reported intensity, duration, number and frequency of sessions for both the index intervention and control intervention(s). For example, physiotherapy treatment is usually administered for several sessions; therefore, it is necessary to assess how many sessions each participant attended. For single‐session interventions (e.g. surgery), this item is irrelevant.
12	Timing of outcome assessment should be identical for all intervention groups and for all primary outcome measures.
13	Other types of biases. For example: ‐When the outcome measures were not valid. There should be evidence from a previous or present scientific study that the primary outcome can be considered valid in the context of the present. ‐Industry‐sponsored trials. The conflict of interest (COI) statement should explicitly state that the researchers have had full possession of the trial process from planning to reporting without funders with potential COI having any possibility to interfere in the process. If, for example, the statistical analyses have been done by a funder with a potential COI, usually ‘unsure’ is scored.

Furlan 2015

Measures of treatment effect

For continuous outcomes, we will estimate pain and function outcomes treatment effects and express these on a common 0‐100 scale as a mean difference (MD) and 95% confidence intervals (CI). For the other continuous outcomes, we will estimate the treatment effects using mean difference (MD) and 95% CI, if studies use the same outcome measure. If studies use different measures for the same outcome, we will quantify treatment effects with standardised mean difference (SMD) and 95% CI. To facilitate interpretation, we will translate pooled SMDs values to the equivalent in commonly used scales using the standard deviation reported in the included studies. For continuous outcomes, we will also 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 it as a percentage. We will calculate the 'number needed to treat for an additional beneficial outcome' (NNTB) for continuous measures using the Wells calculator (available from the Cochrane Musculoskeletal Group Editorial office, www.musculoskeletal.cochrane.org/). We will only calculate NNTB or 'number needed to treat for an additional harmful outcome' (NNTH) for outcomes showing a clinically significant benefit or harm.

For dichotomous outcomes, we will calculate risk ratio (RR) and 95% CI. We will calculate the absolute change from the difference in the risk between the intervention and control group using GRADEpro and express it as a percentage (GRADEpro GDT). We will calculate the relative change as the risk ratio minus 1 and express it as percentage. We will calculate the NNTB or the NNTH from the control group event rate and the risk ratio using the Visual Rx NNT calculator (Cates 2020).

We will use Review Manager 5 (Review Manager) for all analyses. In the Comments column of the 'Summary of findings' table, we will report the absolute percentage difference, the relative percentage change from baseline, and for outcomes that show a clinically significant difference between treatment groups, we will report the NNTB or NNTH.

Unit of analysis issues

The unit of analysis will be the participant for all trials. Where multiple interventions 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 remotely delivered interventions and one usual control). In the event that we identify cross‐over trials, we will extract data from the first phase (prior to cross‐over) of the trial to avoid potential carry‐over effects. If data prior to cross‐over are not available, we will analyse the trial data as recommended in Chapter 23 of the Cochrane Handbook (Higgins 2020). If we identify cluster‐randomised trials, 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 method described in Chapter 23 of the Cochrane Handbook (Higgins 2020). The meta‐analysis using the inflated variances will be performed using the generic inverse‐variance technique.

Dealing with missing data

Where additional data are required, we will contact study authors or sponsor. If we receive no reply within six weeks, we will impute missing data (e.g. standard deviations) using the methods described in the Cochrane Handbook (Higgins 2019a). We will estimate graphical data using the Web Plot Digitizer software (automeris.io/WebPlotDigitizer/). When we think the missing data introduces serious bias or if trials imputed data, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis.

For dichotomous outcomes (e.g. number of withdrawals due to adverse events), we will use the number of participants randomised in the group as the denominator.

For continuous outcomes (e.g. mean change in pain 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 randomised participants in each group at baseline.

We will compute missing standard deviations (SDs) from other statistics such as standard error (SE) values, confidence intervals (CIs) or P values, as recommended in the Cochrane Handbook (Higgins 2019a). If standard deviations cannot be calculated, we will impute them (e.g. from other studies in the meta‐analysis).

Assessment of heterogeneity

Initially, we will investigate 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. First, we will examine these data in the data extraction tables. Then, we will perform a visual inspection of forest plots, looking at the overlap of the confidence intervals to evaluate heterogeneity, and using the I² and Chi² statistical tests.

As recommended in the Cochrane Handbook (Deeks 2019), an I² value of 0% to 40% "might not be important"; 30% to 60% may represent "moderate heterogeneity"; 50% to 90% may represent "substantial heterogeneity"; and 75% to 100% represents "considerable heterogeneity". As noted in the Cochrane Handbook, we will be mindful that the importance of I² depends on: (i) magnitude and direction of effects and (ii) strength of evidence for heterogeneity. We will interpret the Chi² test so that a P value of less than or equal to 0.10 indicates evidence of statistical heterogeneity.

Assessment of reporting biases

We will create and analyse a funnel plot to explore possible small trials biases. We will interpret the funnel plots by analysing the different possible reasons for funnel plot asymmetry as outlined in Section 10.4 of the Cochrane Handbook and relate this to the results of the review (Sterne 2017). 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 section 10.4 of the Cochrane Handbook (Sterne 2017).

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

Data synthesis

We plan to perform meta‐analysis only after first analysing the data extracted from the studies and observing acceptable levels of heterogeneity regarding clinical and methodological diversity. We will present a narrative summary of the studies where meta‐analysis is not possible. We will pool the overall treatment effects using the random‐effects model only where meta‐analysis is meaningful; that is, where the participants, treatments and the underlying clinical question are similar enough for pooling to make sense. We will use alternative synthesis methods, such as summary of effects 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 effects (McKenzie 2019).

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.

Subgroup analysis and investigation of heterogeneity

We plan to do subgroup analyses based upon the type of neck disorders (i.e. non‐specific, myofascial pain syndrome, radiculopathy and WAD grades I, II and III), duration of symptoms (i.e. acute, subacute and chronic), and duration of follow‐up (short‐, medium‐ and long‐term) for each type of technology delivery and outcome. We will also perform a subgroup analysis on telerehabilitation modality (i.e. telephone, website, app, videoconference). We will use the formal test for subgroup interactions in Review Manager 5 (Review Manager).

Sensitivity analysis

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

• Studies we judge as low risk of bias for selection bias.

• Studies we judge as low risk of bias for detection bias.

• Studies we judge as low risk of bias for attrition bias.

If studies are rated as 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 rules for data synthesis and unit of analysis issues as the main analyses.

Interpreting results and reaching conclusions

We will follow the guidelines in Chapter 12 of the Cochrane Handbook for interpreting results (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.

Summary of findings and assessment of the certainty of the evidence

We will prepare 'Summary of findings' (SoF) tables using GRADEpro software (GRADEpro GDT). We will present telerehabilitation versus usual care as the main comparison. In the SoF tables, we will present the outcomes pain, function, quality of life, depression, anxiety, withdrawals due to adverse events and short‐term serious adverse events. The tables will include the treatment effect, assumed risk, certainty of evidence (GRADE) and number of participants for each comparison in the meta‐analysis (one table per comparison).

We will assess the overall certainty of the evidence using the GRADE approach as recommended in the Cochrane Handbook (Schünemann 2018a), and adapted in the updated Cochrane Back and Neck Group (CBN) method guidelines (Furlan 2015). Two reviewers (JF and BS) will independently assess the certainty of the evidence. We will resolve disagreements through discussion or by referral to a third review author (LC) as necessary. The certainty of the evidence will be based upon five main domains, following the GRADE handbook: study design and risk of bias, inconsistency of results, indirectness, imprecision, and other bias (e.g. publication bias). We will report all decisions to downgrade the studies and the certainty of studies using footnotes and we will make comments to aid the reader's understanding of the review where necessary.These are described in detail in Appendix 3.

Further, there may be circumstances where the overall rating for a particular outcome would need to be adjusted as recommended by GRADE guidelines (Guyatt 2013a). For example, if there were so few data that the results were highly susceptible to the random play of chance, or if studies used 'last observation carried forward' (LOCF) analysis imputation in circumstances where there are substantial differences in adverse event withdrawals, one would have no confidence in the result, and would need to downgrade the certainty of the evidence by three levels, to very low certainty evidence. Further, where there were no data reported for one or more outcomes, we would classify the result as very low certainty evidence (Guyatt 2013b).

History

Protocol first published: Issue 3, 2021

Appendices

Appendix 1. MEDLINE search strategy

1. randomized controlled trial.pt.

2. controlled clinical trial.pt.

3. randomized.ab.

4. placebo.ab.

5. clinical trials as topic.sh.

6. randomly.ab.

7. trial.ti.

8. 1 or 2 or 3 or 3 or 4 or 5 or 6 or 7

9. exp animals/ not humans.sh

10. 8 not 9

11. exp Neck/

12. Neck muscles/

13. Brachial Plexus neuritis/

14. brachial plexus/

15. Cervical plexus/

16. Cervical vertebrae/

17. Cervical rib syndrome/

18. Cervical spine injury/

19. neck.mp.

20. cervical.mp.

21. trapezius.,mp.

22. exp Neck Pain/

23. Neck injuries/

24. Neuritis/

25. Brachial Plexus Neuropathies/

26. Torticollis/

27. "neck pain".mp.

28. neck injur*.mp.

29. neck pain*

30. neck injur*

31. "acute cervical pain".mp.

32. "non‐specific neck pain".mp.

33. "nonspecific neck pain".mp

34. neckache.mp.

35. brachialgia.mp.

36. "brachial neuritis".mp.

37. "cervical spine".mp.

38. "cervical pain".mp.

39. cervicodynia.mp.

40. cervicalgia.mp.

41. "cervico brachial neuralgia".ti,ab.

42. "cervicobrachial neuralgia".ti,ab.

43. "brachial neuralgia".mp.

44. exp Injuries/

45. whiplash injury/

46. whiplash.mp.

47. exp Intervertebral disk degeneration/ or intervertebral disk displacement/

48. Disks.mp.

49. Disk.mp.

50. intervertebral disk displacement*.mp.

51. intervertebral disk degeneration*.mp.

52. exp Fibromyalgia/

53. Myofascial pain syndromes/

54. Polyradiculopathy/

55. Radiculopathy/

56. Spinal nerve roots/

57. Spondylitis/ or discitis/

58. Spondylosis/ or spondylolysis/ or spondylolisthesis/

59. Sprains and Strains/

60. Spinal Osteophytosis/

61. Arthritis/

62. neuritis.mp.

63. radiculopathy.mp.

64. radiculitis.mp.

65. spondylosis.mp.

66. spondylitis.mp.

67. spondylolisthesis.mp.

68. or/21‐77

69. telemedicine.mp. or exp Telemedicine/

70. tele*health.mp.

71 tele*care.mp.

72. electronic health.mp.

73. e*health.mp.

74. home*.mp.

75. home*based.mp.

76. mobile*health.mp.

77. mhealth.mp. or m*health.mp.

78. mobile medicine.mp.

79. phone.mp.

80. telephone.mp. or exp Telephone/

81. smart*phone.mp.

82. apps.mp.

83. application program*.mp.

84. application software*.mp.

85. mobile application*.mp. or exp Mobile Applications/

86. mobile communication*.mp.

87. mobile technology.mp.

88. SMS.mp.

89. messaging.mp.

90. text messaging.mp. or exp Text Messaging/

91. texting.mp.

92. exp Internet/ or internet.mp.

93. internet*based.mp.

94. online.mp.

95. web*based.mp.

96. computer based.mp.

97. wireless.mp.

98. video*conferencing.mp. or exp Video*conferencing/

99. tablet device.mp.

100. iPad.mp.

101. iPhone.mp.

102. distance.mp.

103. remotely delivered.mp.

104. self*management.tw

105. manag*:ti,ab,kw

106. self‐car* or “self car*”.ti,ab,kw

107. self‐manag*

108. “self manag*”

109. or/69‐108

110. 10 and 68 and 109

Appendix 2. The TIDieR Checklist

Item number	Item	Where located
		Primary paper (page or appendix number)	Other (details)
	BRIEF NAME
1.	Provide the name or a phrase that describes the intervention.
	WHY
2.	Describe any rationale, theory, or goal of the elements essential to the intervention.
	WHAT
3.	Materials: Describe any physical or informational materials used in the intervention, including those provided to participants or used in intervention delivery or in training of intervention providers. Provide information on where the materials can be accessed (e.g. online appendix, URL).
4.	Procedures: Describe each of the procedures, activities, and/or processes used in the intervention, including any enabling or support activities.
	WHO PROVIDED
5.	For each category of intervention provider (e.g. psychologist, nursing assistant), describe their expertise, background and any specific training given.
	HOW
6.	Describe the modes of delivery (e.g. face‐to‐face or by some other mechanism, such as internet or telephone) of the intervention and whether it was provided individually or in a group.
	WHERE
7.	Describe the type(s) of location(s) where the intervention occurred, including any necessary infrastructure or relevant features.
	WHEN and HOW MUCH
8.	Describe the number of times the intervention was delivered and over what period of time including the number of sessions, their schedule, and their duration, intensity or dose.
	TAILORING
9.	If the intervention was planned to be personalised, titrated or adapted, then describe what, why, when, and how.
	MODIFICATIONS
10.	If the intervention was modified during the course of the study, describe the changes (what, why, when, and how).
	HOW WELL
11.	Planned: If intervention adherence or fidelity was assessed, describe how and by whom, and if any strategies were used to maintain or improve fidelity, describe them.
12.	Actual: If intervention adherence or fidelity was assessed, describe the extent to which the intervention was delivered as planned.

Appendix 3. The GRADE approach to evidence synthesis

The certainty of evidence will be categorized as follows:

• High (⊙⊙⊙⊙): further research is very unlikely to change the confidence in the estimate of effect.

• Moderate (⊙⊙⊙○): further research is likely to have an important impact in the confidence in the estimate of effect.

• Low (⊙⊙○○): further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate.

• Very Low (⊙○○○): any estimate of effect is very uncertain.

The evidence available to answer each sub‐question will be graded on the domains in the following manner:

1. Study design and risk of bias: downgraded by one level if > 25% of the participants were from studies with high risk of bias, that is one or more risk of bias domains judged as high risk, except for performance bias due to the nature of the intervention. We will downgrade by two levels if 50% of participants in the comparison are from studies at high overall risk of bias.

2. Inconsistency: We will evaluate each direct comparison for consistency in the direction and magnitude of the effect sizes from individual trials, considering the width of the prediction interval and magnitude of the heterogeneity parameter. Comparisons will be downgraded one level if important and non‐explained heterogeneity is identified through visual inspection or considerable heterogeneity in the I² test ( > 50%). Additionally, we will downgrade one level any direct comparisons that are implicated in loops with important incoherence or where there is a discrepancy between direct and indirect evidence. Evidence of serious inconsistency (heterogeneity in the I² test > 75%) will be downgraded by two levels.

3. Indirectness: downgraded by one level if > 50% of the target group vary in participants are assessed as being outside the target group. We will not downgrade this domain by two levels.

4. Imprecision: In cases where studies include relatively few participants and few events, and thus have wide confidence intervals around the estimate of the effect, the results are imprecise.
‐ Dichotomous outcomes: A) When there is only one study or when there is more than one study, but the total number of events is < 300, we will downgrade the evidence by one level on this criterion. B) When the 95% confidence interval around the pooled or best estimate of effect includes both (i) no effect and (ii) appreciable benefit or appreciable harm, we will downgrade the evidence by one level. We will downgrade the evidence by two levels when there is imprecision due to both A) and B).
‐ Continuous outcomes: A) When there is only one study or when there is more than one study but the total sample size is < 400, we will downgrade the evidence by one level. B) When the 95% confidence interval around the pooled or best estimate of effect includes no effect and the confidence interval crosses an effect size of SMD = 0.5 or MD > 10% of the scale in either direction, we will downgrade the evidence by one level. We will downgrade the evidence by two levels when there is imprecision due to both A) and B).

5. Publication bias: We will assess publication bias using funnel plots if more than 10 trials are included per comparison. If funnel plots show asymmetry, we will downgrade the certainty of evidence by one level. We will not downgrade this domain by two levels.

We will use the recommendations described in Sections 8.5 and 8.7, and Chapters 11 and 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019b; Schünemann 2018a; Schünemann 2018b). When assessing the overall certainty, we may downgrade the evidence by one level for each factor, up to a maximum of three levels for all factors. If there are very severe problems for any one factor, we may downgrade the evidence by two levels due to that factor alone (Higgins 2019b).

Contributions of authors

Conception and design: Bruno Saragiotto, Tiê Yamato, Chris Maher, Leonardo Costa, Steven Kamper, Blake Dear.
Drafting of the protocol: Junior Fandim, Lisandra Almeida, Bruno Saragiotto and Leonardo Costa.
Critical revision of the protocol for important intellectual content: Chris G Maher, Steven Kamper, Blake Dear.
Final approval of the protocol: all authors.

Sources of support

Internal sources

• None, Other

External sources

• National Health and Medical Research Council (NHMRC), Australia

  CGM holds a research fellowship from the National Health and Medical Research Council (NHMRC)

  SJK holds a research fellowship from the National Health and Medical Research Council (NHMRC)

• São Paulo Research Foundation (FAPESP), Brazil

  BTS has received a research grant from the São Paulo Research Foundation (FAPESP, grant number 2016/24217‐7) to conduct a randomised controlled trial on telerehabilitation for chronic pain.

  TPY holds a research fellowship from the São Paulo Research Foundation (FAPESP), Brazil.

  BFD has received a research grant from the São Paulo Research Foundation (FAPESP‐Brazil, grant number 2016/24217‐7) to conduct a randomised controlled trial on telerehabilitation for chronic pain.

• FAPESP‐Brazil and CNPq, Brazil

  LOPC has received board membership and competitive grants from his work from FAPESP‐Brazil and CNPq‐Brazil for two randomised controlled trials for physiotherapy treatments for back pain patients.

Declarations of interest

Mr Junior Fandim has no relevant interests.

Dr Leonardo Costa has received grants from the National Council for Scientific and Technological Development (CNPq) and the São Paulo Research Foundation (FAPESP) since 2016, none related to the topic of this review. Dr Costa is fully employed as an associate professor at Universidade Cidade de São Paulo since 2010.

Dr Tiê Yamato holds a research fellowship from the São Paulo Research Foundation (FAPESP), Brazil.

Ms Lisandra Almeida has no relevant interests.

Professor Chris Maher has received competitive grants from government agencies and industry to support his research. As an invited speaker at conferences, he has had his expenses covered and also received small gifts such as a box of chocolates or a bottle of wine. He has received honoraria for marking theses, reviewing grants and preparing talks. He is also on the Editorial Board of the Cochrane Back and Neck Group. Editors are required to conduct at least one Cochrane Review to ensure that they are aware of the processes and commitment needed to conduct reviews. Any Editor who is a review author is excluded from editorial decisions on the review in which they are contributors.

Dr Blake Dear is part of a group funded by the Australian Government to provide an online mental health service (www.mindspot.org.au/), which is free to all Australians. He is also part of a group funded by the West Australian Primary Health Alliance to provide an online mental health service (www.ports.org.au/) for the state of Western Australia. He receives no royalties related to these works.

Professor Steven Kamper receives a research fellowship from the National Health and Medical Research Council of Australia.

Dr Bruno Saragiotto has received a research grant from the São Paulo Research Foundation (FAPESP‐Brazil, grant number 2016/24217‐7) to conduct a randomised controlled trial on telerehabilitation for chronic pain.

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