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Cochrane Database of Systematic Reviews Protocol - Intervention

Manual therapy and exercise for lateral elbow pain

Authors' declarations of interest

Version published: 13 June 2018 Version history

https://doi.org/10.1002/14651858.CD013042
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Abstract

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

To assess the benefits and harms of manual therapy and exercise, alone or in combination, compared to placebo, no treatment, or another treatment, in adults with lateral elbow pain.

Background

This review is one of two Cochrane Reviews of physical therapy interventions for lateral elbow pain (or lateral epicondylitis or tennis elbow). In keeping with our reviews of physical therapy interventions for rotator cuff disease and adhesive capsulitis (Page 2014a; Page 2014b; Page 2016a; Page 2016b), we have separated the physical therapy review of lateral elbow pain into two reviews. This review will evaluate the benefits and harms of manual therapy and exercise and a second review will evaluate the benefits and harms of electrotherapy modalities.

Description of the condition

Lateral elbow pain is described by many analogous terms in the literature, including tennis elbow, lateral epicondylitis (or epicondylosis), rowing elbow, tendonitis of the common extensor origin, extensor tendinopathy, and peritendinitis of the elbow. For the purposes of this review, and in keeping with previous Cochrane Reviews for this condition, we will use the term lateral elbow pain.

Lateral elbow pain is a common condition, with a reported prevalence of approximately 1.0% to 1.3% in men and 1.1% to 4.0% in women (Shiri 2011). The overall age‐ and sex‐adjusted annual incidence in the general population has been reported to be 3.4 (95% confidence interval (CI) 3.3 to 3.5) per 1000 in a population‐based historical cohort study in Olmsted County, Minnesota (Sanders 2015). However the incidence appears to have decreased over time from 4.5 per 1000 people in 2000 to 2.4 per 1000 in 2012. In keeping with other studies (Bot 2005), the highest incidence is in the 40‐ to 49‐year age group (9 per 1000), followed by the 50‐ to 59‐year age group (6.9 per 1000). It is slightly more common in women, and the recurrence rate within two years is reported to be 8.5% (Sanders 2015). Based upon a 10% sample, they reported that office workers/secretaries followed by healthcare workers particularly nurses, and construction, maintenance, repair and cleaning workers, were the most commonly affected. The condition also affects people who play tennis or other sports with repetitive arm use (Abrams 2012; Hume 2006; Ranney 1995; Walker‐Bone 2004).

A population‐based study investigating occupational risk factors for lateral epicondylitis found an association with manual work (odds ratio (OR) 4.0, 95% CI 1.9 to 8.4) and in multivariate analyses, repetitive bending/straightening of the elbow for more than an hour a day was independently associated with lateral epicondylitis (OR 2.5, 95% CI 1.2 to 5.5) (Walker‐Bone 2012). A large UK case‐control study found associations between lateral elbow pain and rotator cuff tendinopathy, de Quervains tenosynovitis, carpal tunnel syndrome, oral glucocorticoid use and past smoking (Titchener 2012).

It is thought to be an overload injury at the common extensor origin at the lateral epicondyle (bony bump on lateral side of the elbow, at the bottom of the humerus bone). Pathologic studies have identified the presence of angiofibroblastic hyperplasia (fibroblast proliferation, vascular hyperplasia and disorganised collagen) (Nirschl 1979). The extensor carpi radialis brevis muscle of the forearm and its tendon (at the elbow) seem to become weakened from overuse, resulting in microscopic tears in the tendon where it attaches to the lateral epicondyle, leading to inflammation and pain (AAOS 2015).

People with lateral elbow pain typically present with pain and tenderness over the lateral epicondyle. Repetitive movement, lifting and gripping often aggravate the pain. Examination findings include localised tenderness over the common extensor origin at the lateral epicondyle and elicitation of pain on resisted dorsiflexion of the wrist, middle finger, or both, and loss of grip strength (AAOS 2015).

The acute pain of lateral elbow pain usually lasts six to 12 weeks and is often reported to result in work absence (Mallen 2009). However in the Olmsted County study, in a 10% sample of the whole cohort, only 4% reported missing work (between 1 and 12 weeks), although 16% reported work restrictions; half had no more than one or two visits to their healthcare provider, almost three‐quarters (74%) were no longer seeking care three months after their initial diagnosis; and only a small proportion continued to have symptoms beyond one year (18% who continued to receive care 6 months after first diagnosis had a median duration of care of 844 days). (Sanders 2015). A UK population‐based study, that included adults aged 25 to 64 years, found that in the 5% of adults with epicondylitis (lateral or medial) who took sickness absence because of their elbow symptoms, the median absence was 29 days (Walker‐Bone 2012). For most people it is a self‐limiting condition. Another study found that 80% of participants with pain already greater than four weeks duration, had recovered after one year (without any specific treatment) (Bisset 2006).

Prognostic factors, at least moderately associated with a poorer outcome at one year, include previous occurrence, high physical strain at work, manual jobs, high baseline levels of pain, distress, or both, and less social support. Depression and ineffective coping skills have also been found to strongly predict disability (Alizadehkhaiyat 2007). A recent ultrasound study determined that presence of a lateral collateral ligament tear or large (≥ 6 mm) intrasubstance tears were associated with a poorer outcome, but no relationship between tendon thickness or neovascularity and outcome was seen (Clarke 2010).

Although lateral elbow pain is generally a self‐limiting condition, it results in significant disability, health care utilisation, lost productivity and costs (Silverstein 2006). Therefore, treatment that shortens the duration of symptoms and disability has the potential to be of significant value in terms of reduced morbidity and costs, to both the individual and the community. While many treatments are available for lateral epicondylitis, the optimal evidence‐based treatment remains unclear. Currently available treatments include topical and oral non‐steroidal anti‐inflammatory drugs (NSAIDs) (Pattanittum 2013), orthotic devices (Borkholder 2004; Struijs 2002), physical therapy modalities, such as deep friction massage, exercises, laser and ultrasound therapy (Bisset 2005; Bisset 2006; Bjordal 2008; Herd 2008; Kohia 2008; Smidt 2003), glucocorticoid injection (Assendelft 1996; Coombes 2010; Krogh 2013; Smidt 2002), extracorporeal shock wave therapy (Buchbinder 2005), acupuncture (Green 2002), and surgery (Buchbinder 2002; Lo 2007). Only a small number of people with lateral epicondylitis undergo surgery, although Sanders et al have reported an increase between 2009 to 2011 compared with earlier years (3% of 1186 cases between 2009 and 2011 within two years of diagnosis, compared with about 1% in earlier years (Sanders 2015).

Description of the intervention

Manual therapy and exercise as a treatment for lateral elbow pain are often delivered together, although they can be delivered separately. The interventions can be recommended by primary care physicians but are most commonly delivered by health professionals such as physiotherapists, occupational therapists, chiropractors and osteopaths. Manual therapy involves the movement of a joint or muscle and may include joint mobilisation, manipulation or massage (APA 2015). Exercises are targeted physical activities that aim to improve muscle strength and joint range of motion, and may include stretches to restore muscle length and eccentric exercises to restore structure and function of the muscle‐tendon complex (APA 2015). These may be performed at home or under supervision by a clinician. The goal of manual therapy and exercise for people with lateral elbow pain is primarily to reduce pain and increase function.

How the intervention might work

Manual therapy and exercise may reduce pain and stiffness, and increase joint mobility of the elbow but it is not clear how they might exert these effects for lateral elbow pain, given that the symptoms appear to arise from the point of tendon insertion (Nirschl 1979). However, as the extensor carpi radialis brevis muscle may become weakened with lateral elbow pain, and microscopic tears may form in the tendon where it attaches to the lateral epicondyle (AAOS 2015), physical therapy and exercise may have a role in strengthening the muscle, improving grip strength, and improving blood flow and healing. How this improves pain is not known, but one hypothesis is that the movements stimulate peripheral mechanoreceptors and inhibit nociceptors, thereby reducing pain (Frank 1984).

Why it is important to do this review

Physical therapy is a commonly used intervention for lateral elbow pain (Mallen 2009). Conclusions from previous systematic reviews or commentaries of the benefits of manual therapy and exercise interventions in treating lateral elbow pain are largely inconclusive, or conflicting (Bisset 2005; Herd 2008; Kohia 2008; Smidt 2003).

As previous systematic reviews are inconclusive, and randomised controlled trials (RCTs) have been published subsequent to these reviews (e.g. Bisset 2006 and Peterson 2011), an up‐to‐date systematic review using rigorous Cochrane conduct and reporting methods is justified.

Objectives

To assess the benefits and harms of manual therapy and exercise, alone or in combination, compared to placebo, no treatment, or another treatment, in adults with lateral elbow pain.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs) or controlled clinical trials with quasi‐randomised methods of allocating participants to treatment (such as by alternation, or date of birth or other pseudo‐randomised methods). We will include studies reported as full‐text, those published as abstracts only, and unpublished data. We will not impose any language restrictions.

Types of participants

We will include trials that enrolled adult participants with a diagnosis of lateral elbow pain (as defined by the trial authors). These criteria usually include clinical features, such as pain that is maximal over the lateral epicondyle, and reproducibility of pain by two or more of the following tests: palpation of the lateral epicondyle, or the common extensor origin of the elbow, or both; gripping; and resisted wrist or second or third finger extension (dorsiflexion). They may also include criteria such as the presence of focal hypoechoic areas or frank tears or alterations in the normal fibrillary pattern in the common extensor origin when examined by ultrasound or magnetic resonance imaging (MRI).

We will also include trials that include participants with medial elbow pain or other pain at other tendon insertion sites only if the lateral elbow pain results are presented separately, or at least 90% of participants have lateral elbow pain. We will exclude trials that include participants with a history of significant trauma or inflammatory or degenerative disease such as rheumatoid arthritis or osteoarthritis.

Types of interventions

We will include trials comparing any manual therapy or exercise intervention, or both delivered together, to placebo, no treatment, a different type of manual therapy or exercise, or another active intervention. We will also include trials that combine manual therapy and exercise interventions with electrotherapy interventions. Trials that compare manual therapy and exercise delivered in addition to another active intervention, compared to that active intervention alone, will also be eligible for inclusion.

Manual therapy interventions could include mobilisation, manipulation or massage, or a combination of these. Exercises could be supervised, performed individually or in groups, delivered at home or in other settings, land‐based or water‐based but need to be tailored for lateral elbow pain and not just exercise for general fitness or strength (e.g. swimming).

We will exclude trials primarily evaluating the effect of electrotherapy modalities, such as therapeutic ultrasound, laser therapy, transcutaneous electrical nerve stimulation (TENS), pulsed electromagnetic field therapy, bipolar interferential current, electromyographic biofeedback, phonophoresis, iontophoresis, or shortwave diathermy, as we will include them in a separate Cochrane Review.

Types of outcome measures

Major outcomes

  1. Participant‐reported pain relief of 30% or greater (a moderately clinically important difference).

  2. Mean overall pain (measured by visual analogue scale (VAS), numerical or categorical rating scale, or other scale, including the McGill pain questionnaire).

  3. Mean function or disability, as measured by disease‐specific disability measures, such as the Patient‐Rated Tennis Elbow Evaluation (PRTEE) questionnaire (Rompe 2007), or the upper‐limb specific Disabilities of the Arm, Shoulder and Hand (DASH) outcome questionnaire (Hudak 1996), or other validated or unvalidated measure.

  4. Participant global assessment of treatment success, measure by global rating of treatment satisfaction, such as the Patient Global Impression of Change (PGIC) scale, or as defined by the trialists (e.g. proportion of participants with significant overall improvement).

  5. Quality of life, as measured by generic measures (such as components of the Short Form‐36 (SF‐36)) or disease‐specific tools.

  6. Number of participant withdrawals due to adverse events, or overall withdrawals if the reasons for withdrawals are not reported.

  7. Number of participants experiencing an adverse event.

Minor outcomes

  1. Other pain measures, including participant‐reported pain relief of 50% or greater; proportion achieving pain score below 30/100 mm on a VAS; participant‐reported pain relief of 'much' or 'very much' improved.

  2. Grip strength (preferably pain‐free maximum grip strength).

  3. Number of participants experiencing a serious adverse event (defined as events that are fatal, life‐threatening or lead to hospitilisation).

  4. Return to work.

Timing of outcome assessment

If multiple time points are reported for outcomes that assess benefits of treatment (e.g. pain, function, quality of life, treatment success), we will group outcomes: > 3 weeks; > 3 weeks to 6 weeks (primary time point); > 6 weeks to 3 months, > 3 months to 6 months; > 6 months. If trials include outcomes at more than one time point within these time periods (e.g. 4 weeks and 5 weeks) we will extract the latest time point (e.g. 5 weeks). We will extract return to work, adverse events, withdrawals and serious adverse events at the end of the trials.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases, unrestricted by date or language.

  1. Cochrane Central Register of Controlled Trials (CENTRAL) (via EBM reviews in Ovid).

  2. MEDLINE (Ovid 1946 to present) (Appendix 1).

  3. Embase (Ovid 1947 to present).

Trial registries

We will search the following trial registries for ongoing trials.

  1. ClinicalTrials.gov (clinicaltrials.gov/).

  2. World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) search portal (apps.who.int/trialsearch/).

We will adapt the search strategy developed for MEDLINE as appropriate for use in the other databases.

Searching other resources

We will screen the reference lists of all included primary studies and systematic review articles to identify potentially relevant studies.

Data collection and analysis

Selection of studies

Two review authors will independently review the search results and identify trials that appear to fulfil our inclusion criteria. All articles selected by at least one of the review authors will be retrieved for closer examination. The review authors will not be blinded to the journal or authors. We will resolve disagreement about inclusion or exclusion of individual studies by consensus or if this cannot be reached by involving a third review author. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009), and 'Characteristics of excluded studies' table.

Data extraction and management

Two review authors working independently will extract the following data from the included trials using prepiloted data extraction forms. They will resolve any differences by consensus, or arbitration by a third review author if needed.

  1. Trial characteristics including type (e.g. parallel or cross‐over), country, source of funding, and trial registration status (with registration number recorded if available).

  2. Participant characteristics, including age, sex, duration of symptoms, and inclusion/exclusion criteria.

  3. Intervention characteristics, including type of manual therapy, exercise, or both, and details of the treatments, such as frequency, schedule of treatment, supervision, total number of treatment sessions, use of cointerventions and characteristics of the control intervention.

  4. Outcomes reported, including the measurement scale, direction of the scale, the mean and standard deviation, number of participants per treatment group for continuous outcomes (such as mean pain, function, quality of life), and number of events and number of participants per treatment group for dichotomous outcomes (such as proportion with 30% or more pain relief, treatment success, withdrawals due to adverse events, adverse events) as outlined in 'Types of outcome measures'.

  5. Risk of bias domains as outlined in 'Assessment of risk of bias in included studies'.

  6. Notes: funding for trial, and notable declarations of interest of trial authors.

If outcome data are not reported in a suitable form for meta‐analysis, and where missing data are calculated or estimated from a graph or imputed, we will note this in the 'Characteristics of included studies' tables.

Our a priori decision rules to extract data in the event of multiple outcome reporting in trials are as follows.

  1. Where trialists report both final values and change from baseline values for the same outcome, we plan to extract final values.

  2. Where trialists report both unadjusted and adjusted for baseline values for the same outcome, we plan to extract adjusted values.

  3. Where trialists reported data analysed based on the intention‐to‐treat (ITT) sample and another sample (e.g. per protocol, as‐treated), we plan to extract ITT‐analysed data.

  4. For cross‐over RCTs, we plan to extract data from the first period only.

Where trials do not include a measure of overall pain but include one or more other measures of pain, for the purpose of pooling data, we will combine overall pain with other types of pain in the following hierarchy: unspecified pain; pain at rest; pain with activity; or daytime pain.

Where trialists report multiple pain outcome measures, for the purposes of pooling data, we will extract one measure using the following hierarchy: VAS, numerical or categorical rating scale, McGill pain questionnaire, or other scale.

Where trialists report multiple measures of function or disability, for the purposes of pooling data, we will extract a single measure using the following hierarchy: disease‐specific disability measures such as the Patient‐Rated Tennis Elbow Evaluation (PRTEE) questionnaire (Rompe 2007), or the upper‐limb specific Disabilities of the Arm, Shoulder and Hand (DASH) outcome questionnaire (Hudak 1996), or another measure.

If multiple time points are reported within our time frames (up to 3 weeks, > 3 weeks to 6 weeks; > 6 weeks to 3 months, > 3 months to 6 months; > 6 months, we will extract the latest time point (e.g. if data are reported at 4 weeks, 5 weeks, 3 months and 6 months, we will extract outcomes at 5 weeks, 3 months and 6 months).

Assessment of risk of bias in included studies

Two review authors (AF, RJ) will assess the risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will resolve any disagreements by discussion or by involving a third review author (RB). We will assess the following methodological domains.

  1. Random sequence generation (to determine if the method of generating the randomisation sequence was adequate, such as random number tables, computer‐generated random numbers, minimisation, coin tossing, shuffling of cards and drawing of lots).

  2. Allocation sequence concealment (to determine if adequate methods were used to conceal allocation, such as central randomisation and sequentially numbered, sealed, opaque envelopes).

  3. Blinding of participants and personnel.

  4. Blinding of outcome assessors. We will consider blinding separately for subjective self‐reported outcomes (pain, function, treatment success, quality of life) and objective outcomes (such as withdrawals, adverse events, grip strength). For example, for unblinded outcome assessment, risk of bias for mortality may be different than for a participant‐reported pain scale).

  5. Incomplete outcome data.

  6. Selective outcome reporting.

  7. Other potential threat to validity, such as inappropriate analysis in cross‐over trials, baseline imbalance in important factors, inappropriate or uneven application of cointerventions.

We will grade each potential source of bias as high risk, low risk or unclear risk (either lack of information or uncertainty over the potential for bias). We will present the figures generated by the 'Risk of bias' tool to provide summary assessments of the risk of bias.

Assesment of bias in conducting the 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 review.

Measures of treatment effect

When possible, we will base the analyses on ITT data (outcomes provided for every randomised participant) from the individual trials. For each trial, we will present outcome data as point estimates with mean and standard deviations (SDs) for continuous outcomes and risk ratios (RRs) with corresponding 95% confidence intervals (CIs) for dichotomous outcomes.

For continuous data, we will present results as mean differences (MDs) if possible. However, where different scales are used to measure the same outcome or concept, we will use standardised mean differences (SMDs). We will re‐express the SMD as a MD on a typical scale (e.g. 0 to 10 for mean pain) by multiplying the SMD by a typical among‐person SD (e.g. the SD of the control group at baseline from the most representative trial) (Schünemann 2011b).

In the Comments column of the 'Summary of findings' table, we will report the absolute percentage difference, the relative percentage change from baseline, and the number needed to treat for an additional beneficial outcome (NNTB), or number needed to treat for an additional harmful outcome (NNTH) (we will only provide NNTB and NNTH when the outcome shows a statistically significant difference between treatment groups).

For dichotomous outcomes, such as adverse events, we will calculate the NNTB or 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 CMSG Editorial office, musculoskeletal.cochrane.org/). We will use the minimal clinical important difference (MCID) in the calculation of NNTB or NNTH; we will assume a MCID of 1.5 points in a 10‐point scale for pain; and 10 points on a 100‐point scale for function or disability (Gummesson 2003), for input into the calculator.

For dichotomous outcomes, we will calculate the absolute risk difference using the risk difference statistic in Review Manager 5.3 (Review Manager 2014), and we will express the result as a percentage. For continuous outcomes, we will calculate the absolute benefit as the improvement in the intervention group minus the improvement in the control group (MD), in the original units and express it as a percentage.

We will calculate the relative percentage change for dichotomous data as the Risk Ratio ‐ 1 and express it as a percentage. For continuous outcomes, we will calculate the relative difference as the absolute benefit (MD) divided by the baseline mean of the control group, expressed as a percentage.

Unit of analysis issues

If we identify trials that applied manual therapy and exercise to both arms, but the trialists report outcomes per participant without accounting for the bilateral correlation, we will only report results from one arm where possible.

If we are unable to obtain the data for a single arm, or adjust the outcome data, we will include the data as reported by the trialists and comment on the validity of such analyses, and assess the effect of including such data using sensitivity analyses.

If we identify trials that use a cross‐over design, we will only include data from the first time point.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. manual therapy versus no treatment and corticosteroid injections versus no treatment) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting.

Dealing with missing data

We will contact the trialists where data are missing or incomplete.

For dichotomous outcomes that measure adverse events (e.g. number of withdrawals due to adverse events), we will calculate the withdrawal rate using the number of participants that received treatment as the denominator.

For dichotomous outcomes that measure benefits (e.g. proportion of participants with 30% or more reduction in pain), we will calculate the proportion using the number of randomised subjects 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.

Where possible, we will compute missing SDs from other statistics such as standard errors, CIs or P values, according to the methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). If we cannot calculate SDs, we will impute them (e.g. from other studies in the meta‐analysis). We will clearly describe any assumptions and imputations to handle missing data and we will explore the effect of imputation by sensitivity analyses.

Assessment of heterogeneity

We will first assess included trials for clinical homogeneity in terms of participants, interventions and comparators. For studies that we judged as clinically homogeneous, we will assess and quantify the possible magnitude of inconsistency (i.e. heterogeneity) across studies, using the I2 statistic with a rough guide for interpretation 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 (Deeks 2011). In cases of considerable heterogeneity (defined as I2 ≥ 75%), we will explore the data further by comparing the characteristics of individual studies and any subgroup analyses.

Assessment of reporting biases

In order to determine whether reporting bias is present, we will determine whether the protocol of the trial was published before recruitment of participants for the study, and check if all outcome measures have results reported. For studies published after 1 July 2005, we will screen the clincialtrials.gov and the WHO's ICTRP search portal as described in 'Electronic searches'. We will evaluate whether selective reporting of outcomes is present (outcome reporting bias).

We will compare the fixed‐effect estimate against the random‐effects model to assess the possible presence of small sample bias in the published literature (i.e. in which the intervention effect is more beneficial in smaller studies). In the presence of small sample bias, the random‐effects estimate of the intervention is more beneficial than the fixed‐effect estimate (Sterne 2011). We will further explore the potential for small‐study effects in the main outcomes of the review using funnel plots if at least 10 studies reporting pain are included in a meta‐analysis (Sterne 2011).

Data synthesis

Based upon Cochrane Reviews of similar interventions for adhesive capsulitis and rotator cuff disease (Page 2014a; Page 2016a), we may identify a large number of trials and these will have studied a diverse range of interventions. To ensure that our review provides the most relevant data to inform current management, we will consider the following questions and main comparisons.

  1. Is manual therapy plus exercise (with or without electrotherapy) more effective than placebo, no intervention, or another intervention (e.g. glucocorticoid injection, oral NSAID)?

  2. Is manual therapy plus exercise delivered in addition to another intervention more effective than the other active intervention alone?

  3. Is manual therapy more effective than placebo, no intervention, or another intervention?

  4. Are supervised or home exercises more effective than placebo, no intervention, or another intervention?

  5. Is one type of manual therapy or exercise more effective than another, i.e. (a) one type of manual therapy versus another type of manual therapy, or (b) one type of exercise versus another type of exercise?

We will consider the first two questions as the main questions of the review, as a multimodal intervention comprising manual therapy plus exercise is most reflective of current clinical practice.

We plan to pool results of trials with similar characteristics (participants, interventions, outcome measures and timing of outcome measurement) to provide estimates of benefit and harm. We plan to synthesise effect estimates using a random‐effects meta‐analysis model based on the assumption that clinical and methodological heterogeneity is likely to exist and to have an impact on the results. Where we cannot pool data, we plan to present effect estimates and 95% CIs of each trial in tables and summarise the results in text.

'Summary of findings' table

We will present the major outcomes and comparisons of the review in 'Summary of findings' tables which provide key information concerning the quality of evidence, the magnitude of effect of the interventions examined, and the sum of available data on the outcomes participant‐reported pain relief of 30% or greater; mean overall pain; mean function; participant global assessment of treatment success; quality of life; number of participant withdrawals due to adverse events; and number of participants experiencing an adverse event, as recommended by Cochrane (Schünemann 2011a). We will report the following outcomes at >3 weeks to 6 weeks: participant‐reported pain relief of 30% or greater; mean overall pain; mean function; participant global assessment of treatment success; quality of life. We will report withdrawals and adverse events at last follow‐up. The 'Summary of findings' table includes an overall grading of the evidence related to each of the main outcomes, using the GRADE approach (Schünemann 2011b).

Two review authors will independently assess the quality of the evidence. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of a body of evidence as it relates to the studies which contribute data to the meta‐analyses for the prespecified outcomes, and report the quality of evidence as high, moderate, low, or very low. We will use methods and recommendations described in section 8.5 and 8.7, and chapters 11 and 12, of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a; Schünemann 2011a; Schünemann 2011b). We will use GRADEpro software to prepare the SoF tables (GRADEpro GDT 2015). We will justify all decisions to down‐grade the quality of studies using footnotes and we will make comments to aid the reader's understanding of the review where necessary.

We are unlikely to provide a 'Summary of findings' table for every possible comparison identified, but will address the most relevant comparisons to inform current management.

Thus, we plan the following 'Summary of findings' tables.

  1. Manual therapy and exercise (with or without electrotherapy) versus placebo.

  2. Manual therapy and exercise (with or without electrotherapy) versus common usual treatment: pain medication (e.g. NSAIDs).

  3. Manual therapy and exercise (with or without electrotherapy) versus glucocorticoid injection.

Subgroup analysis and investigation of heterogeneity

If there are sufficient data, we plan to carry out the following subgroup analysis, to assess if pain and function differ between participants who have acute symptoms (defined as 3 months or less) compared to those with symptoms for more than three months. We will use the formal test for subgroup interaction in Review Manager 2014 (Review Manager 2014).

If data stratified by symptom duration are not available, but if there are sufficient continuous data from at least 10 studies, we will consider meta‐regression to assess if symptom duration modifies the effect of the intervention on pain and function (using the Stata statistical package; Stata 2017).

We will restrict these analyses to one or two comparisons: manual therapy plus exercise (with or without electrotherapy) versus placebo or versus the most commonly reported active comparator (e.g. glucocorticoid injection).

Sensitivity analysis

We will investigate the robustness of the treatment effect (pain and function) to potential selection bias and potential detection bias by performing the following sensitivity analyses.

  1. Selection bias: remove the trials that reported inadequate or unclear allocation concealment from the meta‐analysis to see if this changes the overall treatment effect.

  2. Detection bias: remove the trials that reported inadequate or unclear participant blinding from the meta‐analysis to see if this changes the overall treatment effect.

  3. We will assess the effect of including imputed data and data based on assumptions.

We will restrict these analyses to one or two comparisons: manual therapy plus exercise (with or without electrotherapy) versus placebo or versus the most commonly reported active comparator (e.g. glucocorticoid injection).