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Cochrane Database of Systematic Reviews Protocol - Intervention

Shockwave therapy for plantar heel pain (plantar fasciitis)

Authors' declarations of interest

Version published: 25 November 2019 Version history

https://doi.org/10.1002/14651858.CD013490
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Abstract

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

To synthesise the available evidence regarding the benefits and harms of extracorporeal shockwave therapy (focused extracorporeal shockwave therapy and radial pulse therapy) in the treatment of plantar heel pain.

Background

Description of the condition

Plantar heel pain is common in adults, with a reported prevalence ranging from 3.6% to 20.9% (Dunn 2004; Garrow 2004; Hill 2008; Pollack 2015). Its reported prevalence is higher in women than in men (23.3%, 95% confidence interval (CI) 19.0 to 28.3 versus 17.6%, 95% CI 13.2 to 22.9, respectively; Hill 2008). It is also a common presentation in runners, accounting for approximately 8% of all running injuries (Taunton 2002). The most common cause of plantar heel pain is plantar fascitis, which is estimated to affect around 10% of adults during their lifetime (Buchbinder 2004; Hossain 2011; Martin 2014). The term plantar fasciitis is often used interchangeably with plantar heel pain. In this review we will use the term plantar heel pain to refer to plantar fasciitis. Plantar fasciitis is most common in individuals between 40 and 60 years old, but also affects a younger population of habitual runners (Buchbinder 2004). In approximately one‐third of cases, it will be present in both heels (Buchbinder 2004). Differential diagnoses include calcaneal stress fracture, spondyloarthritis manifesting as an enthesitis (inflammation of the site where the muscle attaches into the bone), painful peripheral neuropathies, tarsal tunnel syndrome, lesion of the plantar nerve, tumour, and fascial plantar fibromatosis (non‐cancerous tumour growth in the connective tissue) (Hossain 2011).

The aetiology of plantar fasciitis is not well understood, and is likely to be multifactorial (Buchbinder 2019). The plantar fascia is a thick, fibrous band that connects proximally to the calcaneus and distally to the heads of the five metatarsals, acting as a support across the medial longitudinal arch of the foot. Plantar fasciitis, which is characterised clinically by pain and tenderness in the plantar heel area, most commonly occurs at the origin of the plantar fascia, on the anterior, inferior and medial border of the calcaneus (Gibbon 1999). It is associated with obesity, prolonged standing or jumping, excessive pronation of the feet (flat feet), and ankle equinus (reduction in upward bending motion at the ankle) (Riddle 2003; van Leeuwen 2015). As the condition also has a high prevalence in runners, it has been suggested that one of the primary causes is repetitive microtrauma (Lopes 2012). Those with plantar heel pain may present with calcaneal spurs and plantar fascial thickening on radiographic imaging (Menz 2018). However, while people with heel spurs have a higher prevalence of foot pain, the prevalence of plantar fasciitis is similar to people without heel spurs (Moroney 2014).

In many cases, plantar fasciitis is self‐limiting and will resolve without intervention (Buchbinder 2019). However, a recent five to 15 year longitudinal cohort study found that the risk of having symptomatic plantar fasciitis 10 years after onset of symptoms was 45.6% (Hansen 2018). Studies on the economic burden of plantar fasciitis suggest it is the reason for over a million physician visits per year (Riddle 2004), and costs third‐party payers in the USA as much as 376 million US dollars per year (Riddle 2004; Tong 2010).

Options such as stretching (Digiovanni 2006), prefabricated (non‐custom) orthotics (Landorf 2004), and glucocorticoid injections (McMillan 2012), are favoured as first‐line treatment in primary care. Extracorporeal (i.e. outside the body) shockwave therapy is an additional treatment available to people experiencing heel pain (Crawford 2003).

Description of the intervention

There are two types of extracorporeal shockwave therapy – one type focuses on a specific site (focused extracorporeal shockwave therapy), while the other sends pulses radially (around) the site (radial pulse therapy) (Speed 2014; van der Worp 2013). For both types of therapy, a mechanical device is required to produce the pressure pulses. Three different generator technologies are used for focused extracorporeal shockwave therapy: electrohydraulic (pulse discharges of electricity produced under a liquid); electromagnetic (a physical interaction that occurs between electrically charged particles), and acoustic (sound) waves that use the piezoelectric effect (electric charge produced in response to an applied mechanical stress) (Cheing 2003; Ogden 2001). These machines focus the shock wave approximately 4 to 6 cm apart from the application to the skin (Lohrer 2016). Electrohydraulic machines generate higher‐energy shock waves than electromagnetic and piezoelectric machines (Cheing 2003). Radial pulse therapy is produced by a new generation pneumatic machine (a machine operated by air or gas under pressure) (Lohrer 2016; Marks 2008), and is applied directly to the skin (Lohrer 2016).

In focused extracorporeal shockwave therapy, shock waves are transmitted as single pulsed sound waves generated in water inside an applicator (Schmitz 2015). Shock waves are converted from an electrical energy source into a sound ‘shock’ wave. It is referred to as ‘focused’ as the generated pressure field can be adjusted to converge on a specific point within the body (van der Worp 2013). These waves provide an abrupt, discontinuous change in pressure at the interface of two materials (e.g. soft tissue and bone calcifications) that have different density (acoustic impedance) (van der Worp 2013).

Radial pulse therapy produces pressure waves mechanically, by driving a compressed air projectile within a guiding tube to strike a metal applicator (Lohrer 2016; Schmitz 2015). The waves produced by radial pulse therapy are not ‘shock’ waves as they have a short rise time, a high peak pressure and are non‐linear (Lohrer 2016; van der Worp 2013). Radial pulse therapy waves reach their maximal pressure at the source (where they are released from the machine), rather than at a selected point within the body, and so produce a ‘softer’ or more superficial effect than focused extracorporeal shockwave therapy (Ogden 2001; van der Worp 2013). The distinction between radial pulse therapy as a ‘low‐energy’ form of extracorporeal shockwave therapy and focused extracorporeal shockwave therapy as a ‘high‐energy’ form extracorporeal shockwave therapy is incorrect as they are, in fact, two different technologies (Lohrer 2016; Schmitz 2015).

How the intervention might work

The treatment was first used in 1976 as a non‐surgical method for disintegrating calcified kidney stones (Tefekli 2013), and 15 years later to treat delayed union or non‐union of long bone fractures (Valchanou 1991). In 1996, shockwave therapy was first used in the management of plantar fasciitis, working on the theory that it might improve symptoms by breaking up calcified bone spurs seen on plain imaging (Rompe 1996). However, while heel spurs often co‐exist with plantar fasciitis, they also occur in asymptomatic populations, so it is uncertain whether they have a causal role in the development of plantar heel pain (Osborne 2006; Shmokler 1988). Despite uncertainty around the causes of plantar fasciitis, extracorporeal shockwave therapy is now used in people with heel pain with or without heel spurs.

The mechanism of action of both focused extracorporeal shockwave therapy and radial pulse therapy is poorly understood (Wang 2012). It is proposed that the impulses from both types of therapy have a direct effect on local nerves, an anti‐nociceptive effect referred to as ‘hyperstimulation anaesthesia’ (prevention of the activation of pain receptors) (Barnsley 2001). In addition, it is postulated that focused extracorporeal shockwave therapy impacts directly on tissue calcification, alteration of cell activity through cavitation, acoustic micro‐streaming, alteration of cell membrane permeability and induction of diffusible radicals (Barnsley 2001; Speed 2014).

A number of potential adverse effects from the use of extracorporeal shockwave therapy have been reported. These include pain during treatment, oedema, skin redness, bruising, and temporary paraesthesia (Landorf 2015; Salvioli 2017; Surace 2019). More serious potential side effects include generation and movement of bubbles within tissues leading to tissue damage (Cheing 2003). In addition, direct exposure of nerve and vascular structures may result in damage (Cheing 2003).

There is little convincing evidence of the benefits of shockwave therapy for treating musculoskeletal conditions. Previous Cochrane Reviews indicated that extracorporeal shockwave therapy provides little or no benefit in people with lateral elbow pain (Buchbinder 2005; Buchbinder 2006), and probably little benefit for shoulder pain due to rotator cuff disease (Surace 2019). Earlier systematic reviews found uncertain benefits for heel pain (Crawford 2003; Landorf 2015).

Why it is important to do this review

While extracorporeal shockwave therapy has now been used in the treatment of plantar heel pain for over two decades, there remains no standardisation of technology, technique dose (number of impulses supplied per session), or optimal frequency of application. There is also confusion around terminology, particularly as many studies that refer to the use of ‘low energy’ extracorporeal shockwave therapy are actually using radial pulse therapy (Marks 2008; Rompe 1996).

An earlier Cochrane Review summarised the best available evidence for interventions for the treatment of plantar heel pain, but was withdrawn due to being substantially out of date, with a recommendation that the review be split by intervention category (Crawford 2003). A number of more recent systematic reviews have investigated the benefits of extracorporeal shockwave therapy on heel pain (Aqil 2013; Chang 2012; Lou 2017; Salvioli 2017). These reviews reported conflicting results and conclusions. Three concluded that shockwave therapy is effective (Aqil 2013; Lou 2017; Speed 2014), one concluded that it is safe (Aqil 2013), one could draw no conclusions about its effectiveness (Salvioli 2017), and one concluded that only high‐intensity therapy is effective (Chang 2012). A more recent systematic review and meta‐analysis of various non‐surgical treatments for heel pain concluded that the current evidence is equivocal that extracorporeal shockwave therapy is effective in relieving pain and improving function in the short, medium and long term (Babatunde 2019). However, the review failed to distinguish between radial pulse therapy and focused extracorporeal shockwave therapy, and did not investigate the impact of dosage or intensity on relieving plantar heel pain and improving function (Babatunde 2019). These conflicting conclusions may be due to varying inclusion criteria, unclear rationale for excluding some trials from the analyses, and the failure to account for risk of bias in analyses, in particular the risk of detection and performance bias due to lack of blinding of participants.

There remains no consensus on the appropriate application of these technologies and whether or not effectiveness varies by type of modality (e.g. focused extracorporeal shockwave therapy versus radial pulse therapy impulses). Overall, the effectiveness of both focused therapy and radial pulse therapy in the treatment of plantar fasciitis remains uncertain.

Objectives

To synthesise the available evidence regarding the benefits and harms of extracorporeal shockwave therapy (focused extracorporeal shockwave therapy and radial pulse therapy) in the treatment of plantar heel 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. We will include studies reported as full text, those published as abstract only, and unpublished data. We will not impose any date or language restrictions.

Types of participants

We will include trials that enrolled adult participants (≥ 18 years old) with a diagnosis of plantar heel pain or plantar fasciitis as defined by the trial author, regardless of duration of symptoms. We will exclude trials focusing on children, as the origin of heel pain in this population is most likely different (osteochondrosis) to that in adult populations.

We will exclude studies that include participants with pain in the hindfoot, behind the heel or achilles insertion. We will also exclude studies where plantar heel pain is due to a primary diagnosis of nerve injury or foot fracture. We will exclude trials that include populations with multiple conditions that lead to foot pain, unless the trialists present results separately for the participants with plantar heel pain, or unless participants with other conditions form a minority (defined as < 20%).

Types of interventions

We will include any trials that compare extracorporeal shockwave therapy (either focused extracorporeal shockwave therapy or radial pulse therapy) to placebo, no treatment, a different electrotherapy modality, or another active intervention (more details below). We will include trials that apply one of these modalities using any type of device, at any level of energy, with any number of impulses, any number of treatments sessions, and any number of days between sessions. We will include trials that apply therapy with or without the use of anaesthesia.

We will compare shockwave therapy against:

  1. placebo (e.g. physical block used to prevent the transmission of shock waves, or sub‐therapeutic dose of shock waves provided, e.g. 10 impulses of 0.05 mJ/mm2);

  2. no treatment;

  3. physical therapies, including exercise and stretches;

  4. glucocorticoid injections;

  5. other types of injections (e.g. autologous whole blood or platelet rich plasma);

  6. extracorporeal shockwave therapy versus radial pulse therapy;

  7. higher versus lower doses of shockwave therapy

  8. other treatments, including foot orthoses, night splints, surgery;

  9. shockwave therapy delivered in combination with one or more other treatment(s) versus the other treatment(s) alone or versus different treatment(s).

Types of outcome measures

Major outcomes

We will report the following outcomes measured in primary trials.

  1. Mean overall pain (measured on numerical, categorical or visual analogue pain scales (VAS), or other scale including the pain subscale of the Orthopedic Foot and Ankle Society (AOFAS) ankle‐hindfoot scale (Kltaoka 1994)). If trials did not measure overall pain, we will include other pain measures such as unspecified pain, rest pain, pain with activity, daytime pain, and night‐time pain.

  2. Mean function, as measured by specific disability or function measures such as the Roles and Maudsley Score (Roles 1972), Foot Function Index (FFI) (Budiman‐Mak 1991), Foot Health Status Questionnaire (FHSQ) (Bennett 1998), Maryland Foot Score Orthopedic (Myerson 1986), AOFAS ankle‐hindfoot scale (range of motion subscale) (Kltaoka 1994), Manchester Foot Pain and Disability Index (MFPDI) (Garrow 2000), Foot and Ankle Ability Measure (FAAM) (Martin 2005), Mayo Clinical Scoring System (Tornese 2008), Five level function score (Canyilmaz 2016) or other validated measures.

  3. Participant global assessment of treatment success, measured by a global rating of improvement, 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, 30% or greater improvement in pain).

  4. Quality of life, as measured by generic measures (such as the mental health component of the Short Form‐36 (SF‐36) (Jenkinson 1993).

  5. Number of participant withdrawals due to adverse events.

  6. Number of participants experiencing any adverse event.

Minor outcomes

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

2. Participation in leisure or work activities.

Timing of outcome assessment

We will extract outcomes assessing the benefits of treatment (i.e. pain, function, participant‐related global assessment of treatment success and quality of life) at the following time points:

  • ≤ 6 weeks;

  • > 6 weeks and ≤ 12 weeks;

  • > 12 weeks and ≤ 6 months;

  • > 6 months and ≤ 12 months;

  • > 12 months (if available, we will pool data for 2, 5 and 10 year endpoints separately).

The primary time point will be the second one, i.e. over 6 weeks, up to and including 12 weeks. If the trials measured outcomes at multiple time points (i.e. if a study reported outcomes at four, five and six weeks), we will extract outcomes at the latest possible time point for each period.

Search methods for identification of studies

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL) via Evidence‐Based Medicine Reviews (EBMR) in Ovid, MEDLINE (via OVID) and Embase (via OVID).

We will also conduct a search of ClinicalTrials.gov (www.ClinicalTrials.gov) and the World Health Organization's International Clinical trials Registry Platform (ICTRP) (www.who.int/ictrp/en/).

We will search all databases from their inception to the present, and we will impose no restriction on language of publication.

The search strategies are outline in Appendix 1; Appendix 2; Appendix 3. We created a search strategy for ClinicalTrials.gov (Appendix 4) and the ICTRP (Appendix 5).

Searching other resources

We will check reference lists of all primary studies and review articles for additional references.

We will search for errata or retractions from included studies published in PubMed, and report the date this was done within the review.

Data collection and analysis

Selection of studies

Two review authors (RLJ and MJO) will independently screen titles and abstracts for inclusion of all of the potentially‐relevant 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 or publications of all studies categorised as 'retrieve'. Two review authors (RLJ and MJO) will independently screen the full text to 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 person (RVJ). 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 (Moher 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 we will pilot on at least one study in the review. Two independent review authors (RLJ and MJO) will extract study characteristics from included studies and will resolve any discrepancies by discussion or by consulting a third review author (RVJ) if necessary. We will extract the following study characteristics.

  1. Methods: study design, total duration of study, details of any 'run‐in' period, number of study centres and location, study setting, withdrawals, and date of study

  2. Participants: definition and diagnostic criteria for plantar heel pain, inclusion and exclusion criteria, number recruited and included in analyses at each time point, age, sex, disease duration and severity

  3. Interventions: type of therapy (focused extracorporeal shockwave therapy or radial pulse therapy), professional delivering intervention, model of device, level of energy applied, number of impulses, schedule of treatment, total number of sessions, whether or not the treatment was guided by ultrasound, whether local anaesthesia was used and use of co‐interventions

  4. Control intervention characteristics

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

  6. Characteristics of the design of the trial, as outlined below in the 'Assessment of risk of bias in included studies' section.

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

  8. Any missing data that we received where requested from contacting trialists, and data that we requested but that we did not receive.

Two review authors (RLJ and MJO) will independently extract outcome data from included studies. We will extract the number of events and number of participants per treatment group for dichotomous outcomes, and means, standard deviations and number of participants per treatment group for continuous outcomes. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way, and if we transformed data or estimated it from a graph. We will resolve disagreements by consensus or by involving a third person (RVJ). One review author (RLJ) will transfer data into the Review Manager file (RevMan 2014). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports.

We will use PlotDigitizer (PlotDigitizer) to extract data from graphs or figures, in duplicate.

Our a priori decision rules for extracting data from multiple reported outcomes in trials are as follows.

  1. Where a trial reports multiple pain outcome measures, we will extract one measure using the following hierarchy, based on a previous review (Karjalainen 2019):

    1. overall pain (mean or mean change measured by VAS, numeric or categorical rating scale;

    2. unspecified pain;

    3. rest pain;

    4. pain with activity;

    5. daytime pain;

    6. night‐time pain.

  2. Where a trial reports multiple disability or function outcome measures, we will extract one measure according to the following hierarchy, developed using a mixture of frequency of reporting from a previous review (David 2017), and expert consensus (RLJ, MJO and RB):

    1. Foot Function Index (FFI) (Budiman‐Mak 1991);

    2. Foot Health Status Questionnaire (FHSQ) (Bennett 1998);

    3. Orthopedic Foot and Ankle Society (AOFAS) ankle‐hindfoot scale (range of motion scale) score (Kltaoka 1994);

    4. Roles and Maudsley score (Roles 1972);

    5. Maryland Foot and Ankle score (Myerson 1986);

    6. Manchester Foot Pain and Disability Index (MFPDI) (Garrow 2000);

    7. Foot and Ankle Disability Index ( Foot and Ankle Ability Measure (FAAM) (Martin 2005);

    8. Mayo Clinical Scoring System (Tornese 2008);

    9. other scores as reported in the trials, including five‐level function score (Canyilmaz 2016).

  3. Where trialists report both final values and change from baseline values for the same outcome, we will report final values.

  4. Where trialists report unadjusted and adjusted values for the same outcome are reported, we will report the adjusted values.

  5. If data are analysed based on an intention‐to‐treat (ITT) sample and another sample (e.g. per‐protocol, as‐treated), we will extract ITT data.

  6. For cross‐over RCTs, we will extract data from the first period only.

Assessment of risk of bias in included studies

Two review authors (RLJ and MJO) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). We will resolve any disagreements by discussion or by involving another author (RVJ) if necessary. We will assess the risk of bias according to the following domains.

  1. Random sequence generation

  2. Allocation concealment

  3. Blinding of participants and personnel

  4. Blinding of outcome assessment

  5. Incomplete outcome data

  6. Selective outcome reporting

  7. Other bias, such as inappropriate analysis of cross‐over trials, disparities in important factors measured at baseline, inappropriate or uneven application of co‐interventions.

We will grade each potential source of bias as high, low or unclear risk, and provide a quote from the study report together with a justification for our judgment in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgements across different studies for each of the domains listed. We will consider blinding separately for different key outcomes where necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be different than for a patient‐reported pain scale). We will also consider the impact of missing data by key outcomes.

Where information about 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.

Assessment of bias in conducting the systematic review

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

Measures of treatment effect

We will analyse dichotomous data as risk ratios (RR), or Peto odds ratios (OR) when the outcome is a rare event (approximately less than 10%), and report 95% confidence intervals (CIs). We will analyse continuous data using the mean difference (MD) or standardised mean difference (SMD). We will enter data presented as a scale with a consistent direction of effect across studies.

When different scales are used to measure the same conceptual outcome (e.g. disability), we will calculate SMDs instead, with corresponding 95% CIs. We will back‐translate SMDs to a typical scale (e.g. 0 to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (e.g. the standard deviation of the control group at baseline from the most representative trial) (Schünemann 2017b).

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

For dichotomous outcomes, 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 or NNTH for continuous measures using the Wells calculator (available at the Cochrane Musculoskeletal Editorial office, musculoskeletal.cochrane.org). We will use the minimal clinically important difference (MCID) in the calculation of NNTB or NNTH. Studies of MCID in chronic musculoskeletal pain identify that changes of at least 10% to 23% appear to reflect minimally important changes (Dworkin 2008), with a recent systematic review identifying large heterogeneity between studies (Olsen 2018). A study of pain and function in the heel found that the MCID was 8 on a 100‐point VAS for average pain, 19 on a 100‐point VAS for first step pain, and 13 on a 100‐point scale on the FHSQ (Landorf 2010). On the basis of this research, we will assume an MCID of 1.5 points on a 10‐point scale for foot pain. We will assume an MCID of 10 points on a 100‐point scale for function and quality of life.

For dichotomous outcomes, we will use GRADEpro software to calculate the absolute risk difference as the difference in risks between the intervention and control group (GRADEpro GDT 2015), and express the result as a percentage. For continuous outcomes, we will calculate the absolute benefit in the original units as the improvement in the intervention group minus the improvement in the control group, and express this as a percentage.

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

Unit of analysis issues

If it is relevant to report two comparisons from a single trial in the same meta‐analysis (e.g. one shock wave dose versus another shock wave dose versus placebo), we will combine the two treatment groups, as both regimens are relevant, and compare the combined treatment group to placebo. For dichotomous outcomes, we will sum the sample sizes and the numbers of people with events across the relevant intervention arms, to form a single intervention group. For continuous outcomes, we will combine means and standard deviations using the methods described in Chapter 7 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to form a single intervention group.

We are expecting that cross‐over and cluster designs will be rare. If we identify cluster‐randomised designs that did not adjust for potential unit of analysis issues, we will note this and assess the effect of including studies with potential unit of analysis issues in a sensitivity analysis.

If we identify cross‐over trials, we will extract data from the first phase of the trial to avoid potential carry‐over effects.

When trials report results by feet rather than by participant and no adjustments are possible, we will perform a sensitivity analysis to assess the impact of including such studies with potential unit of analysis issues.

Dealing with missing data

We will contact investigators 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). This will include when it is unclear from the publication whether focused extracorporeal shockwave therapy or radial pulse therapy has been used. 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. Any assumptions and imputations to handle missing data will be clearly described and the effect of imputation will be explored by sensitivity analyses.

For dichotomous outcomes (e.g. Number of participant 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 trial does not present the number of participants analysed for each time point, we will use the number of randomised participants in each group at baseline.

Where possible, we will compute missing standard deviations 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 2011). If we cannot calculate standard deviations, we will impute them (e.g. from other studies in the meta‐analysis).

Assessment of heterogeneity

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

As recommended in theCochrane Handbook for Systematic Reviews of Interventions (Deeks 2017), 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 (Higgins 2011), we will keep in mind that the importance of I2 depends on the magnitude and direction of effects and the strength of evidence for 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 (Deeks 2011). 

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 (Sterne 2011) and relate this to the results of the review. If we obtain more than 10 trials, we will use the funnel plot with effect estimates plotted against standard error of the intervention effect to determine whether small study biases (the intervention effect is more beneficial in smaller studies) are present. We will also examine all other possible reasons for funnel plot asymmetry including selection bias, true heterogeneity, sampling error and the possibility that differences are due to chance (Sterne 2017). We will conduct a sensitivity analysis if there is evidence of small‐study effects. As random‐effects meta‐analysis weights the studies more equally than fixed‐effect analysis, we will compare the two methods; if small sample bias is present, it is more likely that a random‐effects estimate will find a beneficial intervention effect than a fixed‐effect estimate (Sterne 2017).

To assess outcome reporting bias, we will determine whether the protocol of the trial was published prior to participant recruitment, and if so determine whether the trial reported results for all outcome measures. For studies published after 1 July 2005, we will screen the WHO ICTRP portal for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

Data synthesis

We will undertake meta‐analysis for each comparison only where this is meaningful, i.e. if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense. We will pool outcomes with a common intervention and comparator.

We will use a random‐effects model as the default, based on the assumption that clinical diversity is likely to exist and that different studies will estimate different intervention effects.

Main planned comparisons

Our primary comparison will be shockwave therapy versus placebo.

Our other main comparison will be shockwave therapy versus glucocorticoid injection, as there is high certainty evidence for the benefits of this intervention (Crawford 2003).

GRADE and 'Summary of findings' tables

We will create a 'Summary of findings' (SoF) tables for both our primary and other main comparison at the primary endpoint of over six weeks and up to 12 weeks using the following outcomes: mean overall pain, mean function, participant global assessment of treatment success and quality of life. We will report withdrawals due to adverse events and total adverse events for the last follow‐up.

Two review authors (RLJ and MJO) will independently assess the certainty of the evidence. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty 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 certainty of evidence as high, moderate, low, or very low. We will use the 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 2017; Schünemann 2017a; Schünemann 2017b). We will use GRADEpro software version 3, which automatically calculates the absolute per cent change for dichotomous outcomes (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 will provide the NNTB or the NNTH, absolute and relative per cent change in the Comments column of the SoF table as described in the 'Measures of treatment effect' section above.

Subgroup analysis and investigation of heterogeneity

Irrespective of whether or not there are direct head‐to‐head trials of extracorporeal shockwave therapy versus radial pulse therapy, we plan to perform a subgroup analysis including placebo‐controlled trials of these therapies to determine if one is more efficacious in terms of pain and function at the primary time point (> 6 weeks and up to 12 weeks).

We will use the formal test for subgroup interactions in Review Manager (RevMan 2014), and will use caution in the interpretation of subgroup analyses as advised in section 9.6 of the Cochrane Handbook (Deeks 2011). We will also compare the magnitude of the effects between the subgroups by means of assessing the overlap of the CIs of the summary estimate. Non‐overlap of the CIs indicates statistical significance.

Sensitivity analysis

We plan to carry out the following sensitivity analyses to investigate the robustness of the treatment effect to:

  1. the potential for selection bias (lack of adequate allocation concealment);

  2. the potential for detection bias (lack of participant blinding).

We will remove the trials that reported inadequate or unclear allocation concealment and lack of participant blinding from the meta‐analysis of pain and function for the main comparison (shockwave therapy versus placebo), at the primary time point (> 6 weeks and up to 12 weeks) to assess the effect of potential selection and detection biases on pain and function.

Interpreting results and reaching conclusions

We will follow the guidelines in the Cochrane Handbook for Systematic Reviews of Interventions, chapter 12 (Schünemann 2017b), 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.