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Cochrane Database of Systematic Reviews Protocol - Intervention

Electrotherapy modalities for lateral elbow pain

Authors' declarations of interest

Version published: 06 June 2018 Version history

https://doi.org/10.1002/14651858.CD013041
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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 electrotherapy modalities compared with 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 electrotherapy modalities and a second review will evaluate the benefits and harms of manual therapy and exercise.

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

Electrotherapy modalities (also known as electrophysical agents) are types of physical therapy that aim to reduce pain and improve function via an increase in energy (electrical, sound, light, magnetic or thermal) into the body (Hurley 2008; Watson 2008; Watson 2010; Wright 2001). Several electrotherapy modalities exist, including low‐level laser therapy, therapeutic ultrasound, interferential current and transcutaneous electrical nerve stimulation (TENS). They may be delivered by various healthcare providers including physiotherapists, physical therapists, chiropractors and osteopaths (Wright 2001).

People seeking treatment for musculoskeletal conditions usually do not receive a single electrotherapy modality in isolation, but as components of a physiotherapy intervention, most often in combination with manual therapy and exercise (Bisset 2005; Dingemanse 2013; Hanchard 2011; Smidt 2002; Trudel 2004).

How the intervention might work

In general, the proposed mechanisms of action of electrotherapies in reducing pain is via an increase in energy (electrical, sound, light, magnetic or thermal) into the body, thus heating tissue which may increase blood flow and promote healing (Watson 2008; Watson 2010). A description of common electrotherapy modalities and their presumed mechanisms of action are outlined in other Cochrane Reviews of similar interventions for adhesive capsulitis and rotator cuff disease (Page 2014b; Page 2016b), and briefly described for more commonly used modalities, below.

Low‐level laser therapy generates a beam of light which has the potential to deliver light energy to tissue depths below the skin (Bjordal 2010; Peplow 2010). Studies suggest that low‐level laser therapy contributes to pain relief by reducing proinflammatory cytokines and increasing anti‐inflammatory growth factors and cytokines (Bjordal 2006; Peplow 2010).

Therapeutic ultrasound delivers energy to deep tissue sites through ultrasonic waves. The purpose of treatment is to increase tissue temperature and induce non‐thermal physiological changes (such as cell permeability and cell growth), which are believed to promote soft tissue healing and muscle relaxation (Watson 2008).

TENS delivers electrical stimulation via electrodes placed over the intact skin surface near the source of pain to activate underlying nerves (Jones 2009; Sluka 2003). The development of TENS was based on the Gate Control Theory of Pain (Melzack 1965), which suggests that there is a 'gating' mechanism in the spinal cord that regulates the amount of incoming painful stimuli and that stimulation of larger nerve fibres using other stimuli (such as TENS) can 'close the gate' and reduce the perception of pain. Evidence from animal studies suggests that TENS reduces pain cell activity and inhibits pain pathways (Jones 2009).

Two electrotherapy modalities are designed to facilitate delivery of topical medication through the skin (that is transdermal delivery); phonophoresis is administered using a therapeutic ultrasound device (Machet 2002; Watson 2008), and iontophoresis is administered using a low‐intensity electrical current through electrodes placed on the skin (Behl 1989; Kasha 2008; Stefanou 2012).

Why it is important to do this review

Two early systematic reviews summarised the best available evidence on the treatment of lateral epicondylitis, including for electrotherapies up until the early 1990s (Ernst 1994; Labelle 1992). Further trials have been published since then. A more recent review synthesised the available evidence for the effectiveness of electrotherapies for treatment of both medial and lateral epicondylitis (Dingemanse 2013). However, their search was restricted to articles in English and they did not include iontophoresis therapy.

This Cochrane Review will provide an up‐to‐date synthesis of randomised controlled trials that have investigated the benefits and harms of electrotherapies for lateral elbow pain.

Objectives

To assess the benefits and harms of electrotherapy modalities compared with 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 electrotherapy modality to placebo, no treatment, a different electrotherapy modality, or another active intervention. Trials in which electrotherapy modalities are used as an adjunct to another intervention (including added to other physical therapy interventions such as manual therapy or exercise) compared to the other intervention alone will be eligible for inclusion.

Possible electrotherapy modalities include, but may not be limited to: ultrasound, laser therapy, light therapy, bipolar interferential current, transcutaneous electrical nerve stimulation (TENS), pulsed electromagnetic field therapy, iontophoresis and phonophoresis. We will not impose restrictions on technique of delivery nor electrotherapy parameters, such as dose, duration and intensity.

Possible comparators may include, but are not limited to: placebo interventions, topical, oral or injected non‐steroidal anti‐inflammatory drugs (NSAIDs), topical, oral or injected glucocorticoids and other electrotherapy modalities.

Manual therapy interventions such as exercise, mobilisation, massage and manipulation are included 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, as measured by a 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', or similar.

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

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

  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 (MPS and FCB) will independently screen titles and abstracts for inclusion of all the potential studies we identify as a result of the search and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports/publication and two review authors (MPS and MJT) will independently screen the full‐text and identify studies for inclusion, and identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion or, if required, we will consult a third review author (JCB). We will identify and exclude duplicates and 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 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

We will use a data collection form for study characteristics and outcome data which has been piloted on at least one study in the review. 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. We will extract the following study characteristics.

  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. Interventions: characteristics of each electrotherapy modality such as parameters of used appliances, frequency, schedule of treatment, total number of treatment sessions and characteristics of the control interventions.

  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.

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 a graph.

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

Three review authors (MPS, FCB and MJT) will independently assess risk of bias for each study using the criteria outlined in chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will resolve any disagreements by discussion or by involving another review author (JCB). We will assess the risk of bias according to the following 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.

We will grade each potential source of bias as high, low or unclear and 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 judgements across different studies for each of the domains listed. In addition, we will consider the impact of missing data by key outcomes.

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 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

We will present outcome data from each trial 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.

We will analyse dichotomous data as RRs or Peto odds ratios when the outcome is a rare event (approximately less than 10%), and use 95% CIs.

For continuous data, when different scales are used to measure the same conceptual outcome (e.g. disability), we will calculate standardised mean differences (SMD) instead, with corresponding 95% CIs. 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

The unit of analysis will be the participant. If trials report participants with bilateral elbow pain, we will analyse data based on the number of participants, not the number of elbows, if possible.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. electrotherapy modality A versus placebo and electrotherapy modality B versus placebo) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study is identified as abstract only or when data are not available for all participants). Where this is not possible, and the missing data are thought to introduce serious bias, 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 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 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 assess clinical and methodological diversity in terms of participants, interventions and outcomes for the included studies to determine whether a meta‐analysis is appropriate. We will do this by observing such data in the data extraction tables. We will assess statistical heterogeneity by visual inspection of the forest plot to assess for obvious differences in result between the studies, and using the I² and Chi² statistical tests.

As recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011), the interpretation of 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 for Systematic Reviews of Interventions (Deeks 2011), we will keep in mind 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 where P ≤ 0.10 indicates evidence of statistical heterogeneity.

If we identify substantial heterogeneity, we will report it and investigate possible causes by following the recommendations in section 9.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

Assessment of reporting biases

We will create and examine a funnel plot to explore possible small study biases. In interpreting funnel plots, we will examine the different possible reasons for funnel plot asymmetry as outlined in section 10.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b), 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 section 10.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

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 (apps.who.int/trialssearch), for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

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.

  • Are electrotherapy modalities more effective than placebo or no treatment?

  • Do electrotherapy modalities provide additional benefit when added to other physical therapy interventions (e.g. manual therapy or exercise, or both)?

  • Are electrotherapy modalities more effective than standard therapies, such as glucocorticoid injection, NSAIDs, or others?

  • Is one type of electrotherapy modality more effective than another?

As electrotherapy modalities are seldom used in isolation, we consider the first two questions to be the most relevant for clinical practice (and will present these results preferentially over other comparisons in the 'Summary of findings' tables).

We will 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 as the default, based on the assumption that clinical and methodological heterogeneity are likely to exist, and to have an impact on the results.

'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 include the primary time point, > 3 weeks to 6 weeks in the tables, except for withdrawals and adverse events, which we will report at last follow‐up.

Two review authors (MPS, FCB) 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 2011b; Schünemann 2011a; Schünemann 2011b), using GRADEpro GDT software (GRADEpro GDT 2015). We will justify all decisions to downgrade the quality of studies using footnotes and we will make comments to aid reader's understanding of the review where necessary.

We will likely not 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. Electrotherapy versus placebo.

  2. Electrotherapy versus common usual treatment: pain medication (e.g. NSAIDs).

  3. 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 5 (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: electrotherapy versus placebo or versus the most commonly reported active comparator (e.g. glucocorticoid injection).

Sensitivity analysis

We plan to carry out the following sensitivity analyses.

  1. We will assess the robustness of the pain and function results to selection and detection biases, by removing trials in secondary analyses with inadequate or unclear allocation concealment to assess the effect of selection bias; and trials with unclear or inadequate participant blinding to assess the effect of detection bias.

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

Interpreting results and reaching conclusions

We will follow the guidelines in chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011b), for interpreting results 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.