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Cochrane Database of Systematic Reviews Review - Intervention

Physiotherapy for pain and disability in adults with complex regional pain syndrome (CRPS) types I and II

Authors' declarations of interest

Version published: 24 February 2016 Version history

https://doi.org/10.1002/14651858.CD010853.pub2

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Abstract

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Background

Complex regional pain syndrome (CRPS) is a painful and disabling condition that usually manifests in response to trauma or surgery. When it occurs, it is associated with significant pain and disability. It is thought to arise and persist as a consequence of a maladaptive pro‐inflammatory response and disturbances in sympathetically‐mediated vasomotor control, together with maladaptive peripheral and central neuronal plasticity. CRPS can be classified into two types: type I (CRPS I) in which a specific nerve lesion has not been identified, and type II (CRPS II) where there is an identifiable nerve lesion. Guidelines recommend the inclusion of a variety of physiotherapy interventions as part of the multimodal treatment of people with CRPS, although their effectiveness is not known.

Objectives

To determine the effectiveness of physiotherapy interventions for treating the pain and disability associated with CRPS types I and II.

Search methods

We searched the following databases from inception up to 12 February 2015: CENTRAL (the Cochrane Library), MEDLINE, EMBASE, CINAHL, PsycINFO, LILACS, PEDro, Web of Science, DARE and Health Technology Assessments, without language restrictions, for randomised controlled trials (RCTs) of physiotherapy interventions for treating pain and disability in people CRPS. We also searched additional online sources for unpublished trials and trials in progress.

Selection criteria

We included RCTs of physiotherapy interventions (including manual therapy, therapeutic exercise, electrotherapy, physiotherapist‐administered education and cortically directed sensory‐motor rehabilitation strategies) employed in either a stand‐alone fashion or in combination, compared with placebo, no treatment, another intervention or usual care, or of varying physiotherapy interventions compared with each other in adults with CRPS I and II. Our primary outcomes of interest were patient‐centred outcomes of pain intensity and functional disability.

Data collection and analysis

Two review authors independently evaluated those studies identified through the electronic searches for eligibility and subsequently extracted all relevant data from the included RCTs. Two review authors independently performed 'Risk of bias' assessments and rated the quality of the body of evidence for the main outcomes using the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach.

Main results

We included 18 RCTs (739 participants) that tested the effectiveness of a broad range of physiotherapy‐based interventions. Overall, there was a paucity of high quality evidence concerning physiotherapy treatment for pain and disability in people with CRPS I. Most included trials were at 'high' risk of bias (15 trials) and the remainder were at 'unclear' risk of bias (three trials). The quality of the evidence was very low or low for all comparisons, according to the GRADE approach.

We found very low quality evidence that graded motor imagery (GMI; two trials, 49 participants) may be useful for improving pain (0 to 100 VAS) (mean difference (MD) −21.00, 95% CI −31.17 to −10.83) and functional disability (11‐point numerical rating scale) (MD 2.30, 95% CI 1.12 to 3.48), at long‐term (six months) follow‐up, in people with CRPS I compared to usual care plus physiotherapy; very low quality evidence that multimodal physiotherapy (one trial, 135 participants) may be useful for improving 'impairment' at long‐term (12 month) follow‐up compared to a minimal 'social work' intervention; and very low quality evidence that mirror therapy (two trials, 72 participants) provides clinically meaningful improvements in pain (0 to 10 VAS) (MD 3.4, 95% CI −4.71 to −2.09) and function (0 to 5 functional ability subscale of the Wolf Motor Function Test) (MD −2.3, 95% CI −2.88 to −1.72) at long‐term (six month) follow‐up in people with CRPS I post stroke compared to placebo (covered mirror).

There was low to very low quality evidence that tactile discrimination training, stellate ganglion block via ultrasound and pulsed electromagnetic field therapy compared to placebo, and manual lymphatic drainage combined with and compared to either anti‐inflammatories and physical therapy or exercise are not effective for treating pain in the short‐term in people with CRPS I. Laser therapy may provide small clinically insignificant, short‐term, improvements in pain compared to interferential current therapy in people with CRPS I.

Adverse events were only rarely reported in the included trials. No trials including participants with CRPS II met the inclusion criteria of this review.

Authors' conclusions

The best available data show that GMI and mirror therapy may provide clinically meaningful improvements in pain and function in people with CRPS I although the quality of the supporting evidence is very low. Evidence of the effectiveness of multimodal physiotherapy, electrotherapy and manual lymphatic drainage for treating people with CRPS types I and II is generally absent or unclear. Large scale, high quality RCTs are required to test the effectiveness of physiotherapy‐based interventions for treating pain and disability of people with CRPS I and II. Implications for clinical practice and future research are considered.

PICOs

Population
Intervention
Comparison
Outcome

The PICO model is widely used and taught in evidence-based health care as a strategy for formulating questions and search strategies and for characterizing clinical studies or meta-analyses. PICO stands for four different potential components of a clinical question: Patient, Population or Problem; Intervention; Comparison; Outcome.

See more on using PICO in the Cochrane Handbook.

Plain language summary

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Physiotherapy for pain and disability in adults with complex regional pain syndrome (CRPS) types I and II

Background

Complex regional pain syndrome (CRPS) is a painful and disabling condition. Most commonly it affects a person's arm and hand or leg and foot and may occur after a traumatic injury. There are two types of CRPS: CRPS I in which there is no nerve injury, and CRPS II in which there is a nerve injury. Guidelines recommend physiotherapy, which could include different kinds of exercise therapy or electrotherapy for instance, along with other medical treatments for treating the pain and disability associated with CRPS. However, we do not know how well these treatments work.

Review question

Which types of physiotherapy treatment are effective for reducing the pain and disability associated with CRPS in adults?

Study characteristics

We searched for clinical trials of physiotherapy up to 12 February 2015. We included 18 trials that had 739 participants with CRPS I. In most of these trials the participants had CRPS I of the arm and hand. We did not find any clinical trials that included participants with CRPS II.

Key results

Overall we did not find any good quality clinical trials of physiotherapy aimed at reducing the pain and disability of CRPS I in adults. Most included trials were not well designed and contained only small numbers of patients. We did find some low quality trials suggesting that two broadly similar types of rehabilitation training, known as 'graded motor imagery' (GMI) and 'mirror therapy', might be useful for reducing the pain and disability associated with CRPS I after traumatic events or surgery or a stroke. From the limited evidence available it appears that some types of electrotherapy, such as ultrasound and pulsed electromagnetic field therapy, as well as a type of massage therapy known as manual lymphatic drainage, are not effective. Most studies did not report on adverse events and so we do not know if these treatments have any harmful side‐effects.

On the whole, because of the limited number and low quality of available trials for the various physiotherapy treatments, we cannot be sure if any of the physiotherapy treatments we evaluated are effective for treating the pain and disability of CRPS I in adults. It is possible that some treatments, such as GMI or mirror therapy, might be effective. Further high quality clinical trials of physiotherapy are needed in order to find out if any of the different types of physiotherapy treatment are effective at improving pain and disability in people with CRPS.

Authors' conclusions

Implications for practice

It is likely that, in line with contemporary clinical guidelines, physiotherapy and rehabilitation based interventions will continue to be first‐line treatments for people with complex regional pain syndrome (CRPS). In this Cochrane review we have been unable to find compelling evidence of the effectiveness, or lack thereof, of physiotherapy interventions, or to inform an optimal approach to therapy, although very low quality evidence suggests a possible benefit of multimodal physiotherapy, graded motor imagery (GMI) and mirror therapy. The available evidence suggests that applying ultrasound to the stellate ganglion or manual lymphatic drainage (MLD) to the affected limb are unlikely to offer clinical benefit to people with CRPS type I.

Implications for research

Overall, given the existing limitations within the current body of evidence, there is a clear need for further research into physiotherapy interventions in people with CRPS but many challenges remain in addressing this problem. Given the relatively low incidence of CRPS, it is likely to be difficult to recruit adequate numbers of participants to clinical trials. It seems likely that the best chance of addressing this challenge is through multicentre, collaborative research projects aimed at recruiting participants from potentially larger pools of clinical populations. It seems unlikely that it will be possible to generate sufficient evidence to support the many individual modalities currently applied to people with CRPS. In this instance there is a case for taking a pragmatic approach to developing contemporary multi‐modal, individually tailored "best practice" models of physiotherapy care and prioritising trials of these programmes against usual or minimal care. Such trials might provide pragmatic estimates of effectiveness which best reflect the value of guideline recommended practice. Larger replication trials of GMI and mirror therapy would also be useful in order to provide more accurate estimates of treatment effect for these interventions, which current evidence suggests may offer meaningful clinical benefit. Future trials should use established diagnostic criteria, clearly report the type of CRPS under investigation and their design should consider recent recommendations (Busse 2015; Dworkin 2008; Dworkin 2009; Dworkin 2010; Turk 2008a; Turk 2008b) for the design and reporting of trials in chronic pain. This will help to ensure that outcomes, thresholds for clinical importance and study design are optimal and we also highlight the need to measure patient‐focused outcomes over clinically relevant periods of time. Furthermore, future trials should adhere to CONSORT guidance, including that related to the reporting of the development and evaluation of complex interventions (Möhler 2015).

Background

Description of the condition

Complex regional pain syndrome (CRPS) is a persistent, painful and disabling condition that usually, but not exclusively, manifests in response to acute trauma or surgery (Goebel 2011; Shipton 2009). The International Association for the Study of Pain (IASP) introduced the diagnostic label 'CRPS' in the 1990s in order to standardise inconsistencies in terminology and diagnostic criteria (Merskey 1994). Two sub‐categories of CRPS have been described: CRPS type I (CRPS I) (formerly and variously referred to as reflex sympathetic dystrophy (RSD), algodystrophy, Sudek's atrophy) in which no nerve lesion is present and CRPS type II (CRPS II) (formerly referred to as causalgia, algoneurodystrophy), in which a co‐existing nerve lesion (as determined by nerve conduction studies or surgical inspection for example) is present (Coderre 2011; Todorova 2013).

CRPS is characterised by symptoms and signs typically confined to a body region or limb, but which may become more widespread (van Rijn 2011). The diagnostic criteria for CRPS originally proposed by the IASP (Merskey 1994) have since been revised in response to their low specificity and potential to over‐diagnose cases of CRPS. The Budapest criteria proposed by Harden 2010 have enhanced diagnostic accuracy and are now widely accepted (Goebel 2011). The diagnosis of CRPS is clinical (Goebel 2011) and the cardinal features include:

  1. continuing pain disproportionate to any inciting event;

  2. the presence of clusters of various symptoms and signs reflecting sensory (e.g. hyperaesthesia, allodynia), vasomotor (e.g. asymmetries of temperature or skin colour, or both), sudomotor (e.g. oedema or altered sweating or both), motor (e.g. reduced range of motion, tremor) or trophic (e.g. altered hair or nails, or both) disturbances; and

  3. the absence of any other medical diagnosis that might better account for an individual's symptoms and signs.

The pathophysiological mechanisms underlying CRPS are not fully understood (Harden 2010). Current understanding implicates multiple mechanisms including complex contributions from a maladaptive pro‐inflammatory response and a disturbance in sympathetically mediated vasomotor control, together with maladaptive peripheral and central neuronal plasticity (Bruehl 2010; Bruehl 2015; Marinus 2011; Parkitny 2013). Furthermore, mechanisms, and in consequence symptoms and signs, may vary between individuals and within individuals over the time course of the disorder, thus heightening the complexity (Marinus 2011).

The incidence of CRPS is not accurately known but population estimates indicate an incidence of somewhere between five and 26 cases per 100,000 person‐years (Marinus 2011). A likely conservative 11‐year period prevalence rate for CRPS of 20.57 per 100,000 people has been reported (Sandroni 2003). CRPS is three to four times more likely to occur in women than in men, and although it may occur at any time throughout the lifespan it tends to occur more frequently with increasing age (Shipton 2009). Genetic susceptibility may serve as an aetiological risk factor for the development of CRPS (de Rooij 2009). In individuals who develop CRPS after a fracture, intra‐articular fracture, fracture‐dislocation, pre‐existing rheumatoid arthritis, pre‐existing musculoskeletal co‐morbidities (e.g. low‐back pain, arthrosis) (Beerthuizen 2012) and limb immobilisation (Marinus 2011) may increase the risk of its development. Psychological traits, such as depression, anxiety, neuroticism and anger, have so far been discounted as risk factors for the development of CRPS (Beerthuizen 2009: Lohnberg 2013), although further prospective studies are required to substantiate this assertion (Harden 2013).

People with CRPS experience significant suffering and disability (Bruehl 2010; Lohnberg 2013). Preliminary data suggest that interference with activities of daily living, sleep, work and recreation is common and further contributes to a diminished quality of life (Galer 2000; Geertzen 1998; Kemler 2000; Sharma 2009).

Studies into the course of CRPS present contradictory findings. Whilst some studies have reported complete and partial symptom resolution within one year (Sandroni 2003; Zyluk 1998), other studies have indicated more protracted symptoms and impairments lasting from three to nine years (de Mos 2009; Geertzen 1998; Vaneker 2006). In addition, emerging evidence suggests that people with CRPS of an upper limb (which develops less often in response to a fracture) and whose affected limb is colder than the contralateral limb, may experience significantly longer disease duration than people with CRPS of a lower limb (which occurs more commonly after fracture) and whose affected limb is warmer than the contralateral limb (de Mos 2009).

Although guidelines for the treatment of CRPS recommend an interdisciplinary multimodal approach, comprising pharmacological and interventional pain management strategies together with rehabilitation, psychological therapy and educational strategies (Goebel 2012; Harden 2013; Perez 2010; Stanton‐Hicks 2002), determining the optimal approach to therapy remains clinically challenging (Cossins 2013; O'Connell 2013).

Description of the intervention

Guidelines recommend the inclusion of a variety of physiotherapy interventions as part of the multimodal treatment of CRPS (Goebel 2012; Perez 2010; Stanton‐Hicks 2002) but their effectiveness is not known. Physiotherapy has been defined as "the treatment of disorders with physical agents and methods" (Anderson 2002) and for CRPS could include any of the following interventions employed either as stand‐alone interventions or in combination: manual therapy (e.g. mobilisation, manipulation, massage, desensitisation); therapeutic exercise and progressive loading regimens (including hydrotherapy); electrotherapy (e.g. transcutaneous electrical nerve stimulation (TENS), therapeutic ultrasound, interferential, shortwave diathermy, laser); physiotherapist‐administered education (e.g. pain neuroscience education); as well as cortically directed sensory‐motor rehabilitation strategies (e.g. graded motor imagery (GMI), mirror therapy, sensory motor retuning, tactile discrimination training).

How the intervention might work

The precise mechanisms of action through which various physiotherapy interventions are purported to relieve the pain and disability associated with CRPS are not fully understood. Theories underpinning the use of manual therapies to relieve pain include the induction of peripheral or central nervous system‐mediated analgesia, or both (Bialosky 2009; Goats 1994). Therapeutic exercise may induce analgesia, via endorphin‐mediated inhibition (Nijs 2012), and improve function, and by extension disability, by restoring range of movement at affected joints and improving neuromuscular function (Kisner 2002). Theories underlying the use of electrotherapy modalities for pain relief variously include spinal cord‐mediated electro‐analgesia, heat‐ or cold‐mediated analgesia and anti‐inflammatory effects (Atamaz 2012; Robertson 2006). Pain neuroscience education may reduce pain and disability by helping individuals to better understand the biological processes underlying their pain in a way that positively changes pain perceptions and attitudes (Louw 2011). Other rehabilitation strategies, such GMI or mirror therapy, may provide pain relief or increase mobility, or both, by ameliorating maladaptive somatosensory and motor cortex reorganisation (Moseley 2005; Moseley 2012).

Why it is important to do this review

A number of systematic reviews suggest that physiotherapy interventions (e.g. exercise, GMI, TENS) employed in combination with medical management may be beneficial in reducing the pain and disability associated with CRPS (Daly 2009; Smith 2005). However, the inclusion of non‐randomised clinical trials and case series designs, together with the exclusion of studies involving people with CRPS II as well as those published in a language other than English, may have biased these conclusions. Furthermore, the methodologies used for conducting systematic reviews have been substantially revised in recent years, such as those recommended within the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach for describing the strength of the evidence (Balshem 2011), which has not been utilised in previous reviews. Given the limitations of existing systematic reviews, together with the availability of potentially numerous physiotherapy treatment strategies for CRPS, an up‐to‐date systematic review of the evidence from randomised clinical trials for the effectiveness of these interventions may assist clinicians in their treatment choices and inform future clinical guidelines that may be of use to policymakers and those who commission health care for people with CRPS.

Objectives

To determine the effectiveness of physiotherapy interventions for treating pain and disability associated with CRPS types I and II.

Methods

Criteria for considering studies for this review

Types of studies

We included randomised controlled trials (RCTs) (including those of parallel, cluster‐randomised and cross‐over design) published in any language. Translators identified by the Managing Editor of the Cochrane Pain, Palliative and Supportive Care Group evaluated studies published in a language other than English. We excluded studies in which participants were not randomised to intervention groups.

Types of participants

We included trials of adults, aged 18 years or older, diagnosed with CRPS I or II, or with an alternative diagnostic label for these conditions (e.g. RSD, causalgia). We grouped trials according to diagnosis (i.e. CRPS I and II, or mixed). Since the use of formal diagnostic criteria for CRPS is inconsistent across studies (Reinders 2002), we included trials that used established or validated diagnostic criteria, including the Veldman criteria (Veldman 1993), the International Association for the Study of Pain (IASP) criteria (Merskey 1994), Bruehl criteria (Bruehl 1999), Budapest criteria (Harden 2010) and Atkins criteria (Atkins 2010), as well as studies that either predate these criteria or use non‐standard diagnostic criteria.

Types of interventions

We included all randomised controlled comparisons of physiotherapy interventions, employed in either a stand‐alone fashion or in combination, compared with placebo, no treatment, another intervention or usual care, or of varying physiotherapy interventions compared with each other, which were aimed at treating pain or disability, or both, associated with CRPS. We included trials in which non‐physiotherapists (e.g. occupational therapists) delivered such physiotherapy interventions, as defined in 'Description of the intervention', and reported the professional discipline of the clinician delivering the intervention. After the publication of our Cochrane protocol, (Smart 2013) we decided to exclude studies that evaluated non‐physiotherapy based interventions (e.g. pharmacological) in which all arms received the same physiotherapy intervention (differing only in the application of the non‐physiotherapy component) as they are unlikely to offer any insight into the value of physiotherapy management (see Differences between protocol and review).

Types of outcome measures

Primary outcomes

  1. Changes in pain severity/intensity as measured using a visual analogue scale (VAS), numerical rating scale (NRS), verbal rating scale or Likert scale;

  2. changes in disability as measured by validated self‐report questionnaires/scales or functional testing protocols.

We presented and analysed primary outcomes as change on a continuous scale or in a dichotomised format as the proportion of participants in each group who attained a predetermined threshold of improvement. For example, we judged cut‐points from which to interpret the likely clinical importance of (pooled) effect sizes according to provisional criteria proposed in the Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (IMMPACT) consensus statement (Dworkin 2008). Specifically, reductions in pain intensity compared with baseline were judged as follows:

  1. less than 15%: 'no important change';

  2. 15% or more: 'minimally important change';

  3. 30% or more: 'moderately important change';

  4. 50% or more: 'substantially important change'.

We planned to use the cut‐points for 'minimally', 'moderately' and 'substantially’ important changes to generate dichotomous outcomes, the effect size for which we would have expressed as the risk ratio (or relative risk (RR)) but a lack of data did not permit any such analyses.

Secondary outcomes

We planned to analyse the following secondary outcome measures where such data were available:

  1. changes in composite scores for CRPS symptoms;

  2. changes in health‐related quality of life (HRQoL) using any validated tool;

  3. changes in patient global impression of change (PGIC) scales;

  4. incidence/nature of adverse effects.

We planned to analyse and present secondary outcomes as change on a continuous scale or in a dichotomised format but a lack of data did not permit any such analyses. For example, equivalent measures of treatment effect with respect to PGIC have been defined as: 'much' or 'very much' improved (moderate benefit) and very much' improved (substantial benefit) (Dworkin 2008). Future updates may allow such analyses where relevant data are available.

Search methods for identification of studies

Electronic searches

We identified relevant RCTs by electronically searching the following databases:

  1. Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library, Issue 1 of 12, 2015;

  2. Database of Abstracts of Reviews of Effects in the Cochrane Library, Issue 1 of 4 2015;

  3. Health Technology Assessments in the Cochrane Library, Issue 1 of 4 2015;

  4. MEDLINE (OVID) (1966 to 11 February 2015);

  5. EMBASE (OVID) (1974 to 11 February 2015);

  6. CINAHL (EBSCO) (1982 to 11 February 2015);

  7. PsycINFO (OVID) (1806 to 11 February 2015);

  8. LILACS; (1982 to 15 February 2015);

  9. PEDro; (1929 to 15 February 2015);

  10. Web of Science (ISI);(1945 to 15 February 2015).

The Trials Search Co‐ordinator of the Cochrane Pain, Palliative and Supportive Care Group devised the search strategies. She and the review authors ran these searches. We used a combination of controlled vocabulary, i.e. medical subject headings (MeSH) and free‐text terms. The search strategies are in Appendix 1.

Searching other resources

Reference lists

On completion of the electronic searches we searched the reference lists of all eligible studies in order to identify additional relevant studies. In addition we screened the reference lists of key physiotherapy textbooks and previous systematic reviews.

External experts

We sent the list of included trials to a content expert to help identify any additional relevant studies.

Unpublished data

In order to minimise the impact of publication bias we searched the following registers and databases to identify unpublished research as well as research in progress:

  1. OpenGrey (System for Information on Grey Literature in Europe);

  2. Dissertation Abstracts (ProQuest);

  3. National Research Register Archive;

  4. Health Services Research Projects in Progress;

  5. Current Controlled Trials Register (incorporating the meta‐register of controlled trials and the International Standard Randomised Controlled Trial Number);

  6. ClinicalTrials.gov;

  7. International Clinical Trials Registry Platform;

  8. Pan African Clinical Trials Registry;

  9. EU Clinical Trials Register.

Data collection and analysis

Selection of studies

Two review authors (KMS and BMW) independently assessed the titles and abstracts of studies we identified by the search strategy for eligibility. If the eligibility of a trial was unclear from the title and abstract, we assessed the full‐text article. We excluded trials that did not match the inclusion criteria (see the 'Criteria for considering studies for this review' section). We resolved any disagreements between review authors regarding a study's inclusion by discussion. If we could not resolve disagreements, a third review author (NEO) assessed relevant studies and we made a majority decision. Trials were not anonymised prior to assessment. We obtained potentially relevant studies identified in the first round of screening in full text and independently assessed these for inclusion using the same process outlined above. We did not apply any language restrictions.

Data extraction and management

Two review authors (KMS and BMW) independently extracted data from all included trials. We extracted data using a standardised and piloted form. We resolved any discrepancies and disagreements by consensus. In cases where we could not achieve consensus, a third review author (NEO) assessed the trial and we took a majority decision. We extracted the following data from each included trial:

  1. country of origin;

  2. study design;

  3. study population (including diagnosis, diagnostic criteria used, symptom duration, age range, gender split);

  4. type of noxious initiating event: surgery, fracture, crush injury, projectile, stab injury, other or no event;

  5. type of tissue injured: nerve, soft tissue, bone;

  6. presence of medicolegal factors (that may influence the experience of pain and the outcomes of therapeutic interventions);

  7. concomitant treatments that may affect outcome: medication, procedures etc.;

  8. sample size: active and control/comparator groups;

  9. intervention (including type, parameters (e.g. frequency, dose, duration), setting and professional discipline of the clinician delivering the therapy);

  10. type of placebo/comparator intervention;

  11. outcomes (primary and secondary) and time points assessed;

  12. adverse effects;

  13. author conflict of interest statements;

  14. assessment of risk of bias.

Assessment of risk of bias in included studies

We assessed the overall risk of bias for each included trial on the basis of an evaluation of key domains using a modified version of the Cochrane 'Risk of bias' assessment tool. We classified risk of bias as either 'low' (low risk of bias for all key domains), 'unclear' (unclear risk of bias for one or more key domains) or 'high' (high risk of bias for one or more key domains), as outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We also considered experimental design‐specific (e.g. cross‐over study designs) 'Risk of bias' issues where appropriate (Higgins 2011b). We assessed the following key domains of risks of bias for each included trial using either 'yes', 'no' or 'unclear' judgements:

  1. random sequence generation (checking for possible selection bias). We assessed the method used to generate the allocation sequence as either: low risk of bias (any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated); or high risk of bias (studies using a quasi/non‐random process (e.g. odd or even date of birth; hospital or clinic record number);

  2. allocation concealment (checking for possible selection bias). The method used to conceal allocation to group prior to assignment determines whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We assessed the methods used as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes); unclear risk of bias (method not clearly stated); or high risk of bias (studies that do not conceal allocation (e.g. open list));

  3. blinding of study participants and personnel (checking for possible performance bias). We assessed the methods used to blind participants and care providers as either: low risk of bias (participants and care providers blinded to allocated intervention and unlikely that blinding broken; or no/incomplete blinding but judged that both intervention arms reflect active interventions of relatively equal credibility delivered with equal enthusiasm); unclear risk of bias (insufficient information provided to permit a judgement of low/high risk of bias); or high risk of bias (participants and care providers not blinded to the allocated intervention and interventions are clearly identifiable as control and experimental; or participants and care providers blinded to the allocated intervention but likely that blinding was broken);

  4. blinding of outcome assessment (self reported outcomes) (checking for possible detection bias). We assessed the methods used to blind study participants self‐reporting outcomes (e.g. pain severity) from knowledge of which intervention a participant received. We assessed the methods as either: low risk of bias (participants blinded to allocated intervention and unlikely that blinding broken; or no/incomplete blinding but judged that both intervention arms reflect active interventions of relatively equal credibility delivered with equal enthusiasm); unclear risk of bias (insufficient information provided to permit a judgement of low/high risk of bias); or high risk of bias (participants not blinded to the allocated intervention and interventions are clearly identifiable as control and experimental; or participants blinded to the allocated intervention but likely that blinding was broken);

  5. blinding of outcome assessment (investigator‐administered outcomes) (checking for possible detection bias). We assessed the methods used to blind researchers undertaking outcome assessments (e.g. functional testing protocols) from knowledge of which intervention a participant received. We assessed the methods as at either: low risk of bias (researchers blinded to allocated intervention and unlikely that blinding broken); unclear risk of bias (insufficient information provided to permit a judgement of low/high risk of bias); high risk of bias (researchers not blinded to the allocated intervention; or researcher blinded to the allocated intervention but likely that blinding was broken);

  6. incomplete outcome data (drop out) (checking for possible attrition bias). We first assessed for risk of attrition bias by evaluating participant drop out rates according to judgements based on the following criteria: low risk of bias (less than 20% drop out and appears not to be systematic, with numbers for each group and reasons for drop out reported); unclear risk of bias (less than 20% drop out but appears to be systematic or numbers per group and reasons for drop out not reported); high risk of bias (greater than or equal to 20% drop out);

  7. incomplete outcome data (method of analysis) (participants analysed in the group to which they were allocated) (checking for possible attrition bias). We further assessed for risk of attrition bias by separately evaluating the appropriateness of the method of analysis employed, using the following criteria: low risk of bias (participants analysed in the group to which they were allocated (intention‐to‐treat (ITT) or as an available case analysis); unclear risk of bias (insufficient information provided to determine if analysis was based on the principle of ITT or per protocol); or high risk of bias (if per protocol analysis used or where available data is not analysed or participant’s data were included in group to which they were not originally assigned to);

  8. selective reporting (checking for possible reporting bias). We assessed studies for selective outcome reporting using the following judgements: low risk of bias (study protocol available and all pre‐specified primary outcomes of interest adequately reported or study protocol not available but all expected primary outcomes of interest adequately reported or all primary outcomes numerically reported with point estimates and measures of variance for all time points); unclear risk of bias (insufficient information provided to permit a judgement of low/high risk of bias); or high risk of bias (incomplete reporting of pre‐specified primary outcomes or point estimates and measures of variance for one or more primary outcome not reported numerically (e.g. graphically only) or one or more primary outcomes reported using measurements, analysis methods or subsets of data that were not pre‐specified or one or more reported primary outcomes were not pre‐specified or results for a primary outcome expected to have been reported were excluded);

  9. other bias. We assessed studies for other potential sources of bias. We determined judgements regarding low/unclear/high risk of bias according to the potential confounding influence of identified factors, for example: low risk of bias (appears free of other potentially serious sources of bias e.g. no serious study protocol violations identified); unclear risk of bias (other sources of bias may be present but there is either insufficient information to assess whether an important risk of bias exists or insufficient rationale or evidence regarding whether an identified problem will introduce bias); or high risk of bias (results may have been confounded by at least one potentially serious risk of bias, e.g. a significant baseline imbalance between groups; a serious protocol violation; use of 'last observation carried forward' when dealing with missing data).

We also evaluated included trials for the additional sources of bias associated with:

  1. sample size; and

  2. duration of follow‐up, as recommended by Moore 2010.

Small studies are more prone to bias because of their inherent imprecision and due to the effects of publication biases (Dechartres 2013; Moore 2012; Nüesch 2010). Inadequate length of follow‐up may produce an overly positive view of the true clinical effectiveness of interventions, particularly in persistent conditions (Moore 2010). These additional criteria were not considered 'key domains' and therefore did not inform judgements of a trial's overall risk of bias. We assessed these trials according to the following criteria:

  1. sample size (checking for possible biases confounded by small sample size): we assessed trials as being at low risk of bias (greater than or equal to 200 participants per treatment arm); unclear risk of bias (50 to 199 participants per treatment arm); high risk of bias (less than 50 participants per treatment arm);

  2. duration of follow‐up (checking for possible biases confounded by a short duration of follow‐up): we assessed trials as being at low risk of bias (follow‐up of greater than or equal to eight weeks); unclear risk of bias (follow‐up of two to seven weeks); or high risk of bias (follow‐up of less than two weeks).

Two review authors (KMS and BMW) independently undertook the 'Risk of bias' assessments, and resolved any disagreements by discussion. If they could not reach an agreement, a third review author (NEO) undertook a 'Risk of bias' assessment and we took a majority decision.

Measures of treatment effect

We presented treatment effect sizes using appropriate metrics. We calculated the risk ratio (RR) with 95% confidence intervals (CIs) for dichotomised outcome measures, and the number needed to treat (NNT) as an absolute measure of treatment effect where possible.

We expressed the size of treatment effect on pain intensity, as measured with a VAS or NRS, using the mean difference (MD) (where all studies utilised the same measurement scale) or the standardised mean difference (SMD) (where studies used different scales). In order to aid interpretation of the pooled effect size we planned to back‐transform the SMD value to a 0 to 100 mm VAS format on the basis of the mean standard deviation (SD) from trials using a 0 to 100 mm VAS where possible.

We analysed the data using Review Manager (RevMan) (RevMan 2014). We plotted the results of each RCT with available data as point estimates with corresponding 95% CIs and displayed them using forest plots. If included trials demonstrated clinical homogeneity we performed a meta‐analysis to quantify the pooled treatment effect sizes using a random‐effects model. We did not perform a meta‐analysis when clinical heterogeneity was present. Similarly we presented secondary outcomes, though we did not consider them for meta‐analysis.

Unit of analysis issues

All included trials randomised participants at the individual participant level. We planned to meta‐analyse estimates of treatment effect (and their standard errors (SE)) from cluster‐RCTs employing appropriate statistical analyses using the generic inverse‐variance method in RevMan (RevMan 2014), as suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). Where we considered such trials to have employed inappropriate analyses, we planned to utilise methods for 'approximately correct analysis' where possible (Higgins 2011b). In addition, we planned to enter cross‐over trials into a meta‐analysis when it was clear that data were free from carry‐over effects, and to combine the results of cross‐over trials with those of parallel trials by imputing the post‐treatment between‐condition correlation coefficient from an included trial that presented individual participant data and use this to calculate the SE of the SMD. These data may be entered into a meta‐analysis using the generic inverse‐variance method (Higgins 2011b). Issues concerning cluster‐RCTs and crossover trials did not arise as we did not identify any cluster‐RCTs that met the inclusion criteria of this review and we did not conduct any quantitative analyses on the one included crossover trial. We may include such analyses where relevant data are available in future updates of this Cochrane review.

Dealing with missing data

We attempted to contact the authors of included trials when numerical data were unreported or incomplete. If trial authors only presented data in graphical form, we did not attempt to extract the data from the figures. If SD values were missing from follow‐up assessments but were available at baseline, we used these values as estimates of variance in the follow‐up analyses.

Assessment of heterogeneity

We evaluated the included trials for clinical homogeneity regarding study population, treatment procedure, control intervention, timing of follow‐up and outcome measurement. For trials that were sufficiently clinically homogenous to pool, we formally explored heterogeneity using the Chi² test to investigate the statistical significance of any heterogeneity, and the l² statistic to estimate the amount of heterogeneity. Where significant heterogeneity (P value < 0.1) was present, we planned to explore subgroup analyses (see the 'Differences between protocol and review' section).

Assessment of reporting biases

We planned to test for the possible influence of publication bias on trials that utilised dichotomised outcomes by estimating the number of participants in trials with zero effect required to change the NNT to an unacceptably high level (defined as an NNT of 10), as outlined by Moore 2008. An absence of relevant data meant that we did not undertake any analyses. Instead, we considered the possible influence of small study/publication biases on review findings as part of our 'Risk of bias' assessment (see the 'Assessment of risk of bias in included studies' section) and as part of our Grading of Recommendations Assessment, Development and Evaluation (GRADE) assessments (Guyatt 2011a) of the quality of evidence (see the 'Data synthesis' section). We may include such analyses in future updates of this Cochrane review where relevant data are available.

Data synthesis

Where possible, we grouped extracted data according to diagnosis (CRPS types I or II, or mixed), intervention, outcome (i.e. pain, disability) and duration of follow‐up (short‐term: zero to less than two weeks postintervention; mid‐term: two to seven weeks postintervention; and long‐term: eight or more weeks postintervention). Regarding intervention, we planned to pool data from trials that investigated the same single therapy separately for each therapy. We planned to pool trials of multimodal physiotherapy programmes together.

For all analyses, we report the outcome of the 'Risk of bias' assessments. Where we found inadequate data to support statistical pooling, we performed a narrative synthesis of the evidence. We were only able to combine trials through meta‐analysis for one type of intervention (graded motor imagery (GMI)) because of insufficient data and clinical heterogeneity. We conducted a qualitative analysis of all trial findings and used the GRADE approach to assess the quality of evidence (Guyatt 2011a; Guyatt 2011b).

To ensure consistency of GRADE judgements we applied the following criteria to each domain equally for all key comparisons of the primary outcome:

  1. limitations of studies: we downgraded once if more than 25% of the participants were from trials we classified as being at high risk of bias;

  2. inconsistency: we downgraded once if heterogeneity was statistically significant and the I² statistic value was greater than 40%. When a meta‐analysis was not performed we downgraded once if the trials did not show effects in the same direction;

  3. indirectness: we downgraded once if more than 50% of the participants were outside the target group;

  4. imprecision: we downgraded once if there were fewer than 400 participants for continuous data and fewer than 300 events for dichotomous data;

  5. publication bias: we downgraded once where there was direct evidence of publication bias or if estimates of effect based on small scale, industry sponsored studies raised a high index of suspicion of publication bias.

Two review authors (KS and NO) made the judgement of whether these factors were present or not. We considered single trials to be inconsistent and imprecise, unless more than 400 participants were randomised for continuous outcomes or more than 300 for dichotomous outcomes. We applied the following definitions of the quality of the evidence (Balshem 2011):

  1. high quality: we are very confident that the true effect lies close to that of the estimate of the effect;

  2. moderate quality: we are moderately confident in the effect estimate. The true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different;

  3. low quality: our confidence in the effect estimate is limited. The true effect may be substantially different from the estimate of the effect;

  4. very low quality: we have very little confidence in the effect estimate. The true effect is likely to be substantially different from the estimate of effect.

Subgroup analysis and investigation of heterogeneity

We planned to perform subgroup analyses based on the type of CRPS (i.e. I, II or mixed) and its temporal characteristics (i.e. acute (defined as symptoms and signs of CRPS of zero to 12 weeks duration) and chronic (symptoms and signs of CRPS lasting 13 weeks). However, we did not undertake them due to the insufficient number of included trials.

Sensitivity analysis

We planned to perform sensitivity analyses on risk of bias (investigating the influence of excluding studies classified at high risk of bias) and choice of meta‐analysis model (investigating the influence of using a fixed‐effect analysis). We did not perform them as insufficient data were available (see the 'Differences between protocol and review' section).

Results

Description of studies

See the 'Characteristics of included studies' and 'Characteristics of excluded studies' sections.

Results of the search

We conducted the literature search up to 12 February 2015 and identified 990 papers that comprised original research studies, reviews and poster abstracts, of which 744 remained after we removed duplicates. After we screened titles and abstracts, we discarded 702 records because they did not meet the inclusion criteria of this Cochrane review. We retrieved 42 records for full‐text screening. We deemed 21 trial reports from 18 original trials for inclusion (Askin 2014; Aydemir 2006; Cacchio 2009a; Cacchio 2009b; Dimitrijevic 2014; Duman 2009; Durmus 2004; Hazneci 2005; Jeon 2014; Li 2012; Moseley 2004; Moseley 2005; Moseley 2006; Moseley 2009; Mucha 1992; Oerlemans 1999; Schreuders 2014; Severens 1999; Uher 2000). Four published trial manuscripts reported data pertaining to a single included trial (Oerlemans 1999).

One additional trial is awaiting submission for publication (ISRCTN39729827), one trial is available only as a conference abstract (Mete‐Topcuoglu 2010) and we were unable to contact the authors of one registered trial (NCT00625976). These three trials are awaiting classification (see the 'Characteristics of studies awaiting classification' table).

In addition, we identified five ongoing trials (see the 'Characteristics of ongoing studies' section). We have presented a flow diagram outlining the trial screening and selection process (Figure 1). Two review authors (KMS and BMW) reported study details in the 'Characteristics of included studies' and 'Risk of bias' tables for two papers published in the Turkish language (Aydemir 2006; Hazneci 2005) based on an English translation of the original trial report; and one review author (BMW) reported study details in the 'Characteristics of included studies' and 'Risk of bias' tables for two papers published in the German language (Mucha 1992; Uher 2000).

Figure 1
Study flow diagram.

Study flow diagram.

Included studies

We have provided the details of all included trials in the 'Characteristics of included studies' tables. We extracted relevant data from eight included trials (Askin 2014; Aydemir 2006; Cacchio 2009a; Dimitrijevic 2014; Duman 2009; Durmus 2004; Hazneci 2005; Li 2012). We contacted or attempted to contact the corresponding authors of 10 trials on three occasions in order to obtain missing outcomes data (Cacchio 2009b; Jeon 2014; Moseley 2004; Moseley 2005; Moseley 2006; Moseley 2009; Mucha 1992; Oerlemans 1999; Schreuders 2014; Uher 2000). One trial author responded and supplied data for an outcome measure of 'impairment' but we were unable to extract outcome data linked to 'pain intensity' from the supplied data (Oerlemans 1999); one trial author responded stating that they were unable to supply the relevant data (Schreuders 2014); and there was no response from the other trial authors we had contacted.

Design

All included trials were RCTs, and 17 essentially used a parallel‐group design. Whilst the selected participants in three trials crossed over from comparator to intervention groups (Cacchio 2009b; Moseley 2004; Mucha 1992), none employed a true randomised crossover design and we analysed them up to the point of crossover as parallel group‐designs. One trial employed a within‐subject randomised crossover design (Moseley 2009). Twelve trials included two intervention arms (Cacchio 2009a; Dimitrijevic 2014; Duman 2009; Durmus 2004; Hazneci 2005; Jeon 2014; Li 2012; Moseley 2004; Moseley 2006; Mucha 1992; Schreuders 2014; Uher 2000), five trials included three arms (Askin 2014; Aydemir 2006; Cacchio 2009b; Moseley 2005; Oerlemans 1999) and one study used four arms (Moseley 2009). No cluster‐RCTs met the inclusion criteria of this Cochrane review.

Participants

The 18 trials included a total of 739 participants and the total number of participants per trial ranged from 10 to 135. All 18 trials included participants with CRPS I using a range of diagnostic criteria, most commonly using those of Bruehl 1999. There were no trials that included participants with CRPS II. Fourteen trials included participants with CRPS I of the upper limb (Askin 2014; Aydemir 2006; Cacchio 2009a; Cacchio 2009b; Duman 2009; Durmus 2004; Hazneci 2005; Li 2012; Moseley 2004; Moseley 2005; Moseley 2009; Mucha 1992; Oerlemans 1999; Schreuders 2014), two with either upper or lower limb CRPS I (Dimitrijevic 2014; Moseley 2006), one with CRPS I of the lower limb (Uher 2000) and one trial included participants with either upper, lower, multi‐limb or whole body CRPS I (Jeon 2014). Participants developed CRPS I linked to a range of aetiologies including onset post fracture, soft‐tissue injuries, stroke, surgery, carpal tunnel syndrome as well as of idiopathic onset. Participants had acute symptoms (less than or equal to three months) of CRPS I in six trials (Cacchio 2009a; Dimitrijevic 2014; Durmus 2004; Hazneci 2005; Li 2012; Mucha 1992), chronic symptoms (greater than three months) in seven trials (Duman 2009; Jeon 2014; Moseley 2004; Moseley 2005; Moseley 2006; Moseley 2009; Schreuders 2014), a mix of acute and chronic symptoms in two trials (Askin 2014; Oerlemans 1999), and three trials did not report the duration of symptoms (Aydemir 2006; Cacchio 2009b; Uher 2000). Trials were undertaken across a range of geographical locations including: Turkey (N = 5); Australia (N = 4); Italy, Germany, the Netherlands (N = 2 each); China, Serbia, and South Korea (N = 1 each).

Interventions

We have provided a detailed description of the interventions delivered in each included trial in the 'Characteristics of included studies' table. The types of physiotherapy interventions delivered were heterogenous across the included trials and included various electrotherapy modalities (ultrasound, TENS, laser, interferential therapy, pulsed electromagnetic field therapy), cortically‐directed sensory‐motor rehabilitation strategies (GMI, mirror therapy, virtual body swapping, tactile sensory discrimination training), exercise (active, active‐assisted, passive, stretching, strengthening, mobilising, functional; supervised and unsupervised), manual lymphatic drainage (MLD) and pain management advice. Five trials directly compared an active and placebo intervention (Askin 2014; Aydemir 2006; Cacchio 2009a; Cacchio 2009b; Durmus 2004). Six trials evaluated electrotherapy modalities (Askin 2014; Aydemir 2006; Dimitrijevic 2014; Durmus 2004; Hazneci 2005; Mucha 1992), eight trials evaluated cortically‐directed sensory‐motor rehabilitation strategies (Cacchio 2009a; Cacchio 2009b; Jeon 2014; Moseley 2004; Moseley 2005; Moseley 2006; Moseley 2009; Schreuders 2014), two trials evaluated MLD (Duman 2009; Uher 2000) and two trials evaluated general rehabilitation therapies (Li 2012; Oerlemans 1999).

Excluded studies

We have listed the details regarding the 13 trial reports that we excluded in the 'Characteristics of excluded studies' table. The main reasons for exclusion were that the studies were either not RCTs (N = 8), investigated clinically irrelevant outcome measures (N = 2), tested interventions that fell outside the scope of physiotherapy (N = 2) or included participants with mixed aetiologies with only one participant with CRPS I in each of the two arms of the trial (N = 1).

Risk of bias in included studies

We presented a summary of the 'Risk of bias' assessments for all included trials in Figure 2 and Figure 3. We judged the overall risk of bias as being 'high' for 15 trials (Askin 2014; Cacchio 2009a; Cacchio 2009b; Dimitrijevic 2014; Duman 2009; Jeon 2014; Li 2012; Moseley 2004; Moseley 2005; Moseley 2006; Moseley 2009; Mucha 1992; Oerlemans 1999; Schreuders 2014; Uher 2000) and 'unclear' for three trials (Aydemir 2006; Durmus 2004; Hazneci 2005). We did not judge any of the included trials as having an overall 'low' risk of bias.

Figure 2
'Risk of bias' graph: review authors' judgements about each 'Risk of bias' item presented as percentages across all included trials.

'Risk of bias' graph: review authors' judgements about each 'Risk of bias' item presented as percentages across all included trials.

Figure 3
'Risk of bias' summary: review authors' judgements about each 'Risk of bias' item for each included trial.

'Risk of bias' summary: review authors' judgements about each 'Risk of bias' item for each included trial.

Allocation

Only seven out of the 18 trials reported using, or were judged to have used, adequate methods to generate a random sequence and conceal allocation (Aydemir 2006; Dimitrijevic 2014; Li 2012; Moseley 2004; Moseley 2005; Moseley 2006; Schreuders 2014) and as such we judged them as being of 'low' risk of selection bias. The risk of selection bias was 'unclear' in 10 trials (Cacchio 2009a; Cacchio 2009b; Duman 2009; Durmus 2004; Hazneci 2005; Jeon 2014; Moseley 2009; Mucha 1992; Oerlemans 1999; Uher 2000) where the methods used to generate the allocation sequence or where the method of allocation concealment were not adequately reported enough in order to allow a judgement of 'high' or 'low' risk of bias. One trial, Askin 2014, used a quasi‐randomisation method and we judged it as having a 'high' risk of selection bias.

Blinding

We judged six trials to have a 'low' risk of performance bias (Askin 2014; Aydemir 2006; Dimitrijevic 2014; Durmus 2004; Hazneci 2005; Moseley 2005), where participants were adequately blinded to their intervention or where we considered a lack of blinding to have been unlikely to have biased trial outcomes. Eight trials were at 'high' risk of performance bias and consequently detection biases because of inadequate or a lack of blinding (Duman 2009; Li 2012; Moseley 2004; Moseley 2006; Mucha 1992; Oerlemans 1999; Schreuders 2014; Uher 2000). We judged three trials, all of which tested the efficacy of electrotherapy‐based modalities, as at 'low' risk of detection bias because they successfully blinded participants and outcome assessors (Askin 2014; Aydemir 2006; Durmus 2004).

Incomplete outcome data

Twelve trials either had no drop‐outs or a drop‐out rate of less than 20% and as such we judged them as having a 'low' risk of attrition bias secondary to drop‐outs (Askin 2014; Cacchio 2009b; Duman 2009; Durmus 2004; Jeon 2014; Li 2012; Moseley 2004; Moseley 2005; Moseley 2006; Moseley 2009; Mucha 1992; Uher 2000). In five trials the risk of attrition bias was 'unclear' either because the drop‐out rate was not reported (Aydemir 2006; Hazneci 2005) or the drop‐out rate between groups was unequal and the effect of which was uncertain (Cacchio 2009a; Dimitrijevic 2014; Oerlemans 1999). One trial, with an overall drop‐out rate of 44%, had a 'high' risk of attrition bias (Schreuders 2014). We judged 11 trials (Cacchio 2009a; Cacchio 2009b; Duman 2009; Durmus 2004; Jeon 2014; Li 2012; Moseley 2004; Moseley 2006; Moseley 2009; Mucha 1992; Oerlemans 1999), two trials (Aydemir 2006; Hazneci 2005) and five trials (Askin 2014; Dimitrijevic 2014; Moseley 2005; Schreuders 2014; Uher 2000) respectively as being at 'low', 'unclear' and 'high' risk of attrition bias as a consequence of their adopted method of analysis.

Selective reporting

We judged a total of nine trials as being of 'high' risk of reporting bias; three trials because of inadequate or incomplete reporting of primary outcomes, or both (Jeon 2014; Oerlemans 1999; Uher 2000) and six trials because the trial authors presented data in graphical format only, i.e. point estimates with measures of variation were not reported (Cacchio 2009b; Moseley 2004; Moseley 2005; Moseley 2009; Mucha 1992; Schreuders 2014). The other nine trials adequately reported outcome data and we judged them as being at 'low' risk of reporting bias (Askin 2014; Aydemir 2006; Cacchio 2009a; Dimitrijevic 2014; Duman 2009; Durmus 2004; Hazneci 2005; Li 2012; Moseley 2006).

Other potential sources of bias

We considered three trials to be at 'high' risk of other potential sources of bias; one trial because it was published as a 'Letter to the Editor' and not as a full trial report (Cacchio 2009b); one trial because violations of the random sequence generation were permitted (Oerlemans 1999); and one trial because it did not report the baseline data of three participants excluded from the analysis and because of a likely highly significant baseline imbalance in duration of symptoms between groups (Schreuders 2014). The 15 other trials appeared to be free of other potential sources of bias.

Sample size

None of the included trials had intervention arms with 200 or more participants per treatment arm. One trial randomised 60 participants to each trial arm and we judged it as being at 'unclear' risk of bias (Li 2012). The remaining 17 trials had less than 50 participants per trial arm and we judged them as being at 'high' risk of bias based on this criterion.

Duration of follow‐up

Nine trials employed a follow‐up period of less than two weeks and we judged them as being at 'high' risk of bias based on this criterion (Askin 2014; Cacchio 2009b; Dimitrijevic 2014; Durmus 2004; Hazneci 2005; Jeon 2014; Moseley 2009; Mucha 1992; Uher 2000). Six trials employed a follow‐up period of eight or more weeks and we judged them as being at 'low' risk of bias (Cacchio 2009a; Duman 2009; Li 2012; Moseley 2005; Moseley 2006; Oerlemans 1999). Three trials reported a follow‐up period of two to seven weeks and we judged them as being at 'unclear' risk of bias (Aydemir 2006; Moseley 2004; Schreuders 2014).

Effects of interventions

Multimodal physiotherapy

One three‐arm trial, Oerlemans 1999, (135 participants), which we judged as being at 'high' risk of bias based on a number of criteria, compared a physiotherapy programme (pain management advice, relaxation exercises, connective tissue massage, TENS and exercise) plus medical treatment according to a fixed pre‐established protocol, to an occupational therapy (OT) programme (splinting, de‐sensitisation, functional rehabilitation) plus medical management and to a control intervention, described as 'social work' (SW), (attention, advice) plus medical management in participants with CRPS I of the upper limb secondary to mixed aetiologies. The trial authors did not adequately report details regarding the nature of the interventions and did not standardise the number of treatment sessions given with the intensity and frequency of treatment adjusted to the individual needs of participants. The trial authors did not report the overall duration of the treatment periods for each trial group.

According to the trial authors, adjuvant physiotherapy, and to a lesser extent, OT were superior to SW for reducing pain according to all four measures of pain intensity at three months post‐recruitment, and for reducing pain from effort of use of the affected extremity at six months. However, there were no significant between‐group differences for any measure of pain intensity at 12 months follow‐up. Numerical data (i.e. group means and standard deviations (SD) for each time‐point) for the four self‐reported measures of pain intensity (current pain, pain from effort of use of the affected extremity, least and worst pain experienced in the preceding week) were not reported, and the trial authors have not provided these data. Consequently, no further analyses of these measures were possible and we could not determine effect sizes.

Physiotherapy demonstrated a small but statistically significant between‐group improvement in impairment at 12 months compared to SW (impairment level sum score, five to 50 scale; mean difference (MD) 3.7, 95% (CI) −7.13 to −0.27, P = 0.03; but not OT.

The trial authors did not report numerical data from other outcomes of interest, including measures of function (Radboud Skills Questionnaire, modified Greentest, Radboud Dexterity Test), HRQoL (Sickness Impact Profile) and adverse events although Oerlemans 1999 state that there were no between‐group differences in function or well‐being at 12 months follow‐up.

Quality of the evidence

There is very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that physiotherapy plus medical treatment may be more effective at reducing pain at short‐ (three months) but not long‐term follow‐up (12 months) compared to a control intervention of SW and that physiotherapy plus medical treatment may be more effective at reducing impairment compared to SW at long‐term follow‐up in the treatment of CRPS I of the upper limb.

Cortically directed sensory‐motor rehabilitation strategies

Graded Motor Imagery

We included four separate trials of GMI, all of which were small trials (13 to 37 participants) judged to be at 'high' risk of bias. Two trials compared the same GMI protocol to control interventions of standard care (Moseley 2004; Moseley 2006); one compared a different GMI protocol plus conventional treatment (occupational and therapy physiotherapy) to conventional treatment alone (Schreuders 2014); and one compared three different GMI protocols to each another (Moseley 2005).

Moseley 2004 (N = 13) compared a six‐week GMI programme (consisting of two weeks of limb laterality recognition followed by two weeks of imagined movements followed by two weeks of mirror‐box therapy) to 12 weeks of ongoing medical management (predominantly physiotherapy) in participants with longstanding CRPS I of the upper limb post wrist fracture. Moseley 2006 compared the same GMI programme to physical therapy and usual care in a combined cohort of 14 participants with phantom‐limb pain and 37 participants with CRPS I of the upper or lower limb of mixed aetiologies. Schreuders 2014 (N = 18) compared a six‐week GMI programme (consisting of one week of limb laterality recognition, followed by one week of imagined movements, followed by four weeks of mirror‐box therapy) plus conventional care (physiotherapy and OT) to conventional care alone in participants with longstanding CRPS I of the upper limb (aetiology not reported).

Moseley 2004 reported a statistically significant improvement in pain, as measured by the Neuropathic Pain Scale (NPS) at six weeks post‐treatment, in participants that received GMI compared to ongoing medical management. Moseley 2004 reported a NNT to obtain a 50% reduction in the NPS (total score) of three (95% CI 1.4 to 10.1). Moseley 2006 reported statistically significant improvements in pain, as measured by a 0 to 100 VAS, and function, as measured by an 11‐point NRS, immediately postintervention and at six months post‐treatment for the combined cohort of participants with CRPS I and phantom limb pain. At six weeks post‐treatment Schreuders 2014 found no statistically significant differences between groups on any measure of pain intensity or function. None of these trials reported any data about adverse events and did not measure other outcomes of interest, such as composite scoring of symptoms, HRQoL and PGIC.

Moseley 2004, Moseley 2006 and Schreuders 2014 presented data for changes in pain and function in participants specifically with CRPS I graphically only and did not report numerical data (i.e. group means and SD values at each time‐point) for measures of pain intensity or function, or both. However, 0 to 100 VAS pain and function data were available from Moseley 2004 and the CRPS I participants in Moseley 2006 from a previous overview of systematic reviews of interventions for CRPS (O'Connell 2013). We used these data in this Cochrane review with the authors' permission. Pooling of these results gave an effect size (weighted mean difference) of −14.45 (95% CI −23.02 to −5.87, P = 0.001, 49 participants, two trials; Analysis 1.1) with no significant heterogeneity. We expressed this data as a percentage of the mean baseline pain levels in the larger trial (58 out of 100), which equated to a 25% (95% CI 10 to 40) reduction in pain intensity at the end of the treatment period. Moseley 2004 presented outcomes at medium‐term follow‐up (six weeks post‐treatment, N = 13, MD −20.00, 95% CI −7.97 to −32.13, P = 0.001). This equated to an improvement of 34% (95% CI 14 to 55) of the baseline VAS pain level in the Moseley 2006 trial (average baseline data for pain VAS was not available from the Moseley 2004 trial report). At long‐term follow‐up (six months post‐treatment (N = 36)) in Moseley 2006, the MD was −21.00, 95% CI −10.83 to −31.17, P < 0.001, which equates to an improvement of 36% (95% CI 19% to 54%). The immediate post‐treatment effect was below the threshold for a moderately clinically important difference but exceeded the threshold for a minimally clinically important difference. The medium‐ and long‐term effects met the threshold for a moderately important benefit. We were unable to obtain numerical data from Schreuders 2014.

We pooled the data on function from two trials (Moseley 2004 and Moseley 2006; data on CRPS I participants only), which returned a MD of: 1.87 (95% CI 1.03 to 2.71, 49 participants, two trials; P < 0.001; Analysis 1.2) at the end of treatment; 2.26 (95% CI 1.42 to 3.10, P < 0.001) at medium‐term follow‐up (Moseley 2004, N = 13); and 2.30 (95% CI 1.12 to 3.48, P < 0.001) at long‐term follow‐up (Moseley 2006, N = 36). This represented a large improvement in function from the baseline function score (0.5) in the control group of the larger trial (Moseley 2006).

In a three‐arm trial, Moseley 2005 (N = 20) compared a six‐week GMI programme with its three components delivered in the 'correct’ order (i.e. two weeks of laterality recognition followed by two weeks of imagined movements followed by two weeks of mirror‐box therapy) to two other GMI programmes with selected components delivered in different orders at odds with its hypothesised mechanism of action, in participants with longstanding CRPS I of the upper limb post wrist fracture. We found statistically significant improvements in pain and function in the correctly ordered GMI group compared to both comparison groups, as measured by the NPS and an 11‐point NRS respectively at 12 weeks post‐treatment. Moseley 2005 reported that at 12‐week follow‐up, the mean reduction in NPS score for the correctly ordered GMI group was approximately seven and 18 points greater than the mean reductions in the other two groups respectively. The trial did not report numerical data for measures of pain intensity and function, and we have been unable to obtain these data from the trial author. Consequently we were unable to perform any further analyses of these measures and we could not determine the effect sizes. The trial did not report any data concerning adverse events and did not measure other outcomes of interest, such as composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that GMI plus medical management may be more effective at reducing pain and improving function than conventional physiotherapy plus medical management in the treatment of CRPS I of the upper limb. There is very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that appropriately ordered GMI was more effective at reducing pain and improving function than inappropriately ordered GMI.

Mirror therapy

We included two trials of mirror therapy (Cacchio 2009a; Cacchio 2009b). Cacchio 2009a (N = 48) compared four weeks of mirror therapy plus conventional stroke rehabilitation to placebo mirror therapy (covered mirror) plus conventional stroke rehabilitation in participants with CRPS I of the upper limb post‐stroke. In a trial judged to be at 'unclear' risk of bias, Cacchio 2009a reported statistically significant improvements in pain and function, at all post‐treatment time‐points, in the mirror therapy group compared to the placebo group. Specifically, Cacchio 2009a reported a mean between‐group difference following treatment in pain at rest (0 to 10 VAS) of −2.9 (95% CI −4.23 to −1.57, P < 0.001) and in pain on movement (shoulder flexion) of −3.10 (95% CI −4.28 to −1.92, P < 0.001). At six‐month follow‐up the differences were still present, −3.4 (95% CI −4.71 to −2.09, P < 0.001) for pain at rest, and −3.8 (95% CI −4.96 to −2.64, P < 0.001) for pain on movement. The post‐treatment and six‐months follow‐up mean differences for pain at rest equated to a 38% (95% CI 21 to 56%) and 45% (95% CI 28 to 62%) reduction in the average baseline pain level respectively, whist the post‐treatment and six‐months follow‐up mean differences for pain on movement equated to a 36% (95% CI 23 to 50%) and 45% (95% CI 31 to 58%) reduction in the average baseline pain level respectively, consistent with a moderately important benefit.

Regarding disability, Cacchio 2009a also reported significant mean between‐group differences in functional limitation, as measured by the functional ability subscale of the Wolf Motor Function Test (WMFT, zero to five score range) of −1.9 (95% CI −2.36 to −1.44, P < 0.001) at the end of treatment and of −2.3 (95% CI −2.88 to −1.72, P < 0.001) at six‐months follow‐up.

In a separate three‐arm trial, judged to be at 'high' risk of bias, Cacchio 2009b (N = 24) compared four weeks of mirror therapy to either placebo mirror therapy (covered mirror) or mental imagery training in participants with CRPS I of the upper limb post stroke. Cacchio 2009b reported that seven out of eight participants in the mirror therapy group reported reduced pain (median change in zero to 100 VAS of −51 mm, range −70 to −18) compared with one of eight participants in the covered mirror therapy group and two of eight participants in the mental imagery group; the median change was not reported for either the covered mirror or mental imagery groups. At the end of the treatment period, pain scores were significantly lower in the mirror therapy group compared to the other two groups. However, the trial authors did not report any further between‐group data and we have been unable to obtain these data from the trial authors. Consequently we were unable to perform any further analyses of these measures and we could not determine the effect size. The trial authors did not report data from other outcomes of interest, including measures of function and adverse events, while they did not measure outcomes, such as composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There was very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision, once for indirectness) that mirror therapy reduced pain and improved upper limb function in participants with post stroke CRPS I of the upper limb compared with covered mirror therapy.

Virtual body swapping

We included one trial of virtual body swapping with mental rehearsal compared to virtual body swapping alone (Jeon 2014) (N = 10) in participants with CRPS I of either the upper or lower limbs, multiple limbs or the whole body, the aetiology of which was not reported. Participants underwent a single session of their allocated intervention with follow‐up immediately post‐treatment only. Jeon 2014 reported that there was no difference between the groups regarding pain intensity, as measured by an 11‐point Likert rating scale ranging from zero (no pain) to 10 (severe pain) immediately post‐treatment. The trial authors did not report numerical data for measures of pain intensity, and we have been unable to obtain these data from the trial authors. As a result, we could not conduct any further analyses and we could not determine the effect size. We rated the trial as at 'unclear' risk of bias for random sequence generation and allocation concealment, and at 'high' risk of bias for selective outcome reporting. The trial authors did not report any data concerning adverse events and did not measure other outcomes of interest, such as measures of function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There was very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that virtual body swapping with mental rehearsal does not reduce pain in people with CRPS I in the short‐term.

Tactile discrimination training

We included one trial, Moseley 2009, that compared four tactile discrimination training (TDT) protocols with one another (N = 10) in participants with CRPS I of the upper limb from mixed aetiologies. Moseley 2009 reported no significant differences in self‐reported pain intensity (0 to 100 VAS) at two day follow‐up. The trial authors did not report numerical data for measures of pain intensity, and they have not supplied us with these data. Thus we were unable to perform any further analyses and we could not determine the effect size. We rated the trial at 'high' risk of bias for selective outcome reporting, sample size and duration of follow‐up. Regarding adverse events, three participants reported that the pressure stimuli associated with the TDT occasionally hurt but that this was not enough to necessitate modification or cessation of the TDT training. The trial authors did not measure other outcomes of interest, such as function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There was very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that TDT does not reduce the pain associated with CRPS I at short‐term follow‐up.

Electrotherapy interventions

Ultrasound of the stellate ganglion versus placebo

Two trials, Askin 2014 and Aydemir 2006, investigated the effectiveness of applying ultrasound directed to the stellate ganglion versus placebo. Both trials were small, with fewer than 50 participants, and were at 'high' or 'unclear' risk of bias based on a number of criteria. Askin 2014 (N = 45) compared two doses (3.0 watts and 0.5 watts intensity) of high frequency ultrasound to placebo ultrasound. All trial groups also received multimodal conventional treatment that included a course of medication (including vitamin C, gabapentin and prednisolone) and physiotherapy (including TENS, contrast baths, active and passive range of motion exercises and stretching, resistance and mirror box exercises). The participants received treatments daily for 20 days. Aydemir 2006 (N = 25) compared stellate ganglion block with ultrasound to blocks with lidocaine and placebo conditions for both interventions. All trial groups received exercises, TENS, contrast baths, compression and oral paracetamol. While only one trial, Aydemir 2006, provided data in an extractable format for meta‐analysis, both trials demonstrated no statistically significant difference of ultrasound over placebo for pain. Regarding assessment of function, Askin 2014 used the DASH score to measure function. While Askin 2014 did not present data in a format extractable for meta‐analysis, they reported no statistically significant effect of ultrasound. Aydemir 2006 measured hand function using a Functional Hand Scale (0 to 19 scale, with lower scores indicating better function) and reported statistically significant improvements in all three trial groups post‐treatment and at one month follow‐up. According to our analyses there were significantly greater improvements in the placebo group post‐treatment (MD 7.86, 95% CI 1.93 to 13.79, P = 0.009) and at one month follow‐up (MD 6.79, 95% CI 0.85 to 12.73, P = 0.02). The trial authors did not present any data concerning adverse events and did not measure other outcomes of interest, such as composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is low quality evidence (RCT evidence: downgrade once for methodological limitations and once for imprecision) that stellate ganglion block via ultrasound is not effective for the treatment of pain or loss of hand function in people with CRPS I.

Ultrasound of the stellate ganglion versus TENS.

One trial with 30 participants compared ultrasound of the stellate ganglion to TENS in military recruits with acute (mean duration of symptoms: 44 days) CRPS I of the upper limb secondary to mixed aetiologies (Hazneci 2005). Both groups also received contrast baths and physiotherapist prescribed exercises. In this trial the ultrasound group demonstrated inferior post‐treatment pain scores (0 to 10 VAS; MD 2.13, 95% CI 1.47 to 2.79, P < 0.001) which equates to a potentially clinically important difference of 27% (95% CI 19 to 36) of the average baseline pain score. The trial authors measured pain severity at the end of the three‐week intervention period only without longer‐term follow‐up. We rated the trial at 'unclear' risk of bias for random sequence generation and allocation concealment. They did not report any data concerning adverse events and did not measure other outcomes of interest, such as function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is low quality evidence (RCT evidence: high, downgraded once for imprecision and once for inconsistency) that ultrasound to the stellate ganglion is inferior to TENS for the treatment of pain in people with CRPS I in the short‐term.

Pulsed electromagnetic field therapy

One trial with 40 participants, Durmus 2004, compared pulsed electromagnetic field (PEMF) treatment (100 Gauss, 50 Hz, five times weekly for six weeks) plus calcitonin and a stretching exercise routine to placebo EMF plus calcitonin and stretching in participants with acute (mean duration of symptoms: 52 days) CRPS I of the upper limb following Colles fracture. At the end of treatment, Durmus 2004 found no statistically significant between‐group difference in pain at rest (VAS), pain on activity, or range of motion. We rated the trial at 'high' risk of bias for study size and duration of follow‐up and at 'unclear' risk of bias for allocation concealment. The trial authors did not report any data concerning adverse events and did not measure other outcomes of interest, such as function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is low quality evidence (RCT evidence: high, downgraded once for imprecision and once for inconsistency) that PEMF is not superior to placebo for the treatment of pain or range of motion in people with CRPS I.

Laser therapy versus Interferential therapy

One trial with 50 participants compared 20 sessions of low‐level laser therapy with interferential current therapy in participants with post‐traumatic CRPS I of the upper or lower limb (Dimitrijevic 2014). Both trial groups also received kinesitherapy that consisted of individualised active and active assisted exercises, strictly dosed up to pain threshold. We rated the trial at 'high' risk of bias for incomplete outcome data, trial size and duration of follow‐up. Post‐therapy the results demonstrated a statistically significant between‐group mean difference for pain at rest (0 to 100 VAS) of −8.6 (95% CI −16.27 to −0.93, P = 0.03) in favour of laser therapy. This equates to a difference of 14% (95% CI 1.5 to 26) from the mean baseline pain score of the two groups, which falls below our criteria for a minimal clinically important difference. There was no statistically significant post‐treatment between‐group difference with respect to pain with movement of the affected wrist or ankle according to our analysis (P = 0.07). The trial authors reported that there were no negative effects of therapy recorded. The trial authors did not measure other outcomes of interest, such as function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that low level laser therapy does not result in a clinically important reduction in pain when compared to interferential therapy when added to exercise therapy.

CO2 Bath therapy

One trial, Mucha 1992, with 40 participants compared carbon dioxide (CO2) baths in addition to exercise therapy with exercise therapy alone in participants with post‐traumatic CRPS I of the hand. Neither intervention is clearly described in the paper though the baths were administered in 12‐minute sessions five times a week for four weeks. Mucha 1992 reported that there was a statistically significant between‐group difference in pain at rest, pain with movement and night pain in favour of the CO2 bath group. The trial authors did not report numerical data, and we have been unable to obtain these data from the trial authors. Consequently, we were unable to perform any further analyses of these measures and could not determine an effect size. We rated the study at 'high' risk of bias on five separate criteria. The trial authors did not report any data concerning adverse events and did not measure other outcomes of interest, such as function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for inconsistency) that CO2 baths combined with exercise therapy are more effective for relieving the pain associated with CRPS I than exercise alone.

Electro‐acupuncture and massage versus rehabilitation

One trial, Li 2012, with 120 participants compared 30 sessions of electro‐acupuncture combined with upper limb massage therapy to 30 sessions of rehabilitation in participants with post stroke shoulder‐hand syndrome. Rehabilitation consisted of active‐assisted scapular movements, Bobath exercises to clench the fist, functional transfer training and proprioceptive neuromuscular facilitation (PNF) exercise. It is unclear if the primary aim of the rehabilitation offered was to manage the shoulder‐hand syndrome explicitly or if it was a general rehabilitation programme aimed at addressing the motor impairments related to the stroke. This trial measured pain in the shoulder when it was taken passively to 90° of elevation but did not include any other measure of upper limb or hand pain. We rated the trial at 'high' risk of bias for blinding of participants and at 'unclear' risk of bias for sample size. Li 2012 reported greater reductions on the outcome pain (in the shoulder when taken passively to 90º) in favour of the electro‐acupuncture and massage group at the end of the six‐week treatment period (MD −1.70, 95% CI −2.09 to −1.31, P = 0.01) which were sustained at 12‐weeks follow‐up (MD −1.40, 95% CI −1.78 to −1.02, P < 0.001). The post‐treatment and 12‐week follow‐up MD values equated to a 21% (95% CI 16 to 26%) and 18% (95% CI 13 to 22%) reduction in the average baseline pain level respectively. These were below the threshold for a moderately clinically important difference but exceeded the IMMPACT threshold (15%) for a minimally important benefit. Li 2012 reported no statistically significant difference in hand function between the two trial groups, but a statistically significant difference in upper limb function in favour of the electro‐acupuncture and massage group at the end of treatment (MD 4.5, 95% CI 0.85 to 8.15, P = 0.05) which was no longer significant at 12‐weeks follow‐up. The trial authors reported that there were no adverse reactions to intervention in either trial group. They did not measure other outcomes of interest, such as composite scoring of symptoms, HRQoL and PGIC. Notably, we also have some concerns regarding the diagnostic equivalence of 'shoulder‐hand syndrome' and CRPS I and whether the control intervention was directed towards the management of the shoulder‐hand syndrome or the upper limb functional stroke problem, both of which may have implications for the generalisability of this trial's findings.

Quality of the evidence

There is very low quality evidence (RCT evidence: high, downgraded once for methodological limitations, once for imprecision and once for indirectness) that a course of electro‐acupuncture and massage is superior to rehabilitation therapy for pain on passive shoulder elevation in participants with post stroke shoulder‐hand syndrome, but not hand‐specific function. Also, the magnitude of effect on pain severity was clinically minimal.

Other interventions

Manual Lymphatic Drainage therapy

Two included trials, Duman 2009 and Uher 2000, investigated the effectiveness of adding MLD therapy to rehabilitation. Duman 2009 (N = 34) compared the addition of MLD massage to conventional care (nonsteroidal anti‐inflammatory drugs and physical therapy) to conventional care alone in participants with CRPS I of the upper limb of mixed aetiology. Uher 2000 (N = 40) compared the addition of MLD in addition to exercise therapy to exercise therapy alone in participants with CRPS I of the lower limb of mixed aetiology. We rated both trials as being at 'high' risk of bias on multiple criteria. We were only able to extract data on relevant outcomes from Duman 2009, but both trials demonstrated no statistically significant effect of the addition of MLD on pain. The trial authors did not report any data on adverse events and did not measure other outcomes of interest, such as function, composite scoring of symptoms, HRQoL and PGIC.

Quality of the evidence

There is low quality evidence (RCT evidence: high, downgraded once for methodological limitations and once for imprecision) that the addition of MLD to rehabilitation does not improve pain in people with CRPS I.

Discussion

Summary of main results

Given the paucity of high quality of evidence derived from our analyses of the 18 included randomised controlled trials (RCTs) (739 participants), we cannot draw any firm conclusions regarding the effectiveness or harmfulness of a broad range of physiotherapy‐based interventions for treating the pain and disability associated with complex regional pain syndrome (CRPS) I in adults.

The results of one included trial, Oerlemans 1999, provided very low quality evidence that a multimodal physiotherapy programme may provide a small, long‐term improvement in impairment, as measured by a composite scoring method, compared to a minimal intervention of ‘social work’, but the magnitude of this effect is of questionable clinical significance. We could not determine its effect on a range of pain‐related outcomes.

Evidence that supports the use of cortically‐directed sensory‐motor rehabilitation strategies was mixed. Our findings suggest that graded motor imagery (GMI) may provide clinically meaningful medium‐ and long‐term improvements in both pain and disability in people with CRPS I, although the results from these trials were from very low quality studies and were inconsistent. While our meta‐analysis of two trials, Moseley 2004 and Moseley 2006, provided evidence of such benefits, we were unable to obtain and include data from one, as yet unpublished, clinical trial with contradictory results (Schreuders 2014); these results should therefore be treated with caution.

Based on two included trials we found very low quality evidence that mirror therapy provides long‐term clinically meaningful improvements in pain and function in people with CRPS I following stroke (Cacchio 2009a; Cacchio 2009b). The effectiveness of mirror therapy in broader participant populations with CRPS I (e.g. post‐trauma) is unknown. We also found very low quality evidence that the more novel interventions of virtual body swapping ± mental rehearsal (Jeon 2014) and tactile discrimination training (TDT) (Moseley 2009) do not provide any short‐term benefits for pain in people with CRPS I.

Evidence that supported the use of electrotherapy‐based interventions was mixed. There was low to very low quality evidence that:

  1. stellate ganglion block via ultrasound combined with a conventional treatment programme was not superior to placebo ultrasound for pain and hand function at medium‐term follow‐up (Askin 2014; Aydemir 2006);

  2. stellate ganglion block via ultrasound combined with contrast baths and exercise was inferior to TENS combined with contrast baths and exercise for pain and short‐term follow‐up (Hazneci 2005);

  3. PEMF therapy was not superior to placebo PEMF for pain at short‐term follow‐up (Durmus 2004);

  4. laser therapy combined with exercise may provide a small, probably clinically insignificant, benefit in pain compared to interferential current therapy and exercise at short‐term follow‐up (Dimitrijevic 2014); and

  5. CO2 bath therapy combined with exercise may improve pain compared to exercise therapy alone although the effect size could not be determined (Mucha 1992) and the interventions were inadequately described.

Two RCTs provided low quality evidence that manual lymphatic drainage (MLD) combined with and compared to either non‐steroidal anti‐inflammatories and physical therapy (Duman 2009) or exercise therapy (Uher 2000) is not beneficial for pain in people with CRPS I.

We found very low quality evidence from one trial, Li 2012, that electro‐acupuncture and massage were superior to a stroke rehabilitation programme for pain on passive shoulder movement in shoulder‐hand syndrome post stroke at longer‐term follow‐up. However, the magnitude of this effect was unlikely to be clinically important and both the reliability and validity of the outcome measure used are questionable.

Only two trial reports, one related to laser and interferential therapies, Dimitrijevic 2014, and one to TDT, Moseley 2009, commented on the presence or absence of adverse events and reported no serious events.

We did not find any clinical trials that included participants with CRPS II that met the inclusion criteria of this Cochrane review.

Overall, we identified a lack of high or moderate quality evidence with which to inform or guide rehabilitation practice in people with CRPS I or II. Based on the current body of evidence, we cannot draw any accurate or firm conclusions regarding the effectiveness or safety of any of the specific physiotherapy‐based interventions we identified in this Cochrane review.

Overall completeness and applicability of evidence

The evidence base for the use of physiotherapy interventions in CRPS is incomplete, although this reflects a broader problem for all intervention research in CRPS (O'Connell 2013). Most included trials (16/18) used established diagnostic criteria to identify participants with CRPS I. However, as might be expected given the development history of such criteria in CRPS, there was some variation in the criteria used between included trials. Beyond various issues relating to risk of bias and study size (see Quality of the evidence) there are very few instances where more than one included trial tested a specific intervention. Two trials, Duman 2009 and Hazneci 2005, specifically recruited participants from military populations. As such, it is possible that contextual factors specific to that participant group and environment may limit the applicability of those results to civilian clinical practice. Eight trials only measured outcomes immediately at the end of treatment with no longer‐term follow‐up. Such trials offer limited information about the genuine clinical utility of interventions for a condition that is commonly persistent. The broad heterogeneity of interventions assessed in the included trials afforded us limited opportunities to pool data. However, it is possible that advances in meta‐analytical statistics may permit such analyses in the future (Melendez‐Torres 2015).

The aim of this Cochrane review was to investIgate the effectiveness of physiotherapy interventions for people with CRPS I or II. We used a deliberately inclusive definition to attempt to include evidence on any intervention that might reasonably be delivered within a physiotherapy context for people with CRPS. As a result the included trials varied considerably but most were designed to test the specific effectiveness of individual modalities either alone, when added to other treatments or compared to other treatments. While these trials offered information about the specific or additional clinical benefits of those modalities, they are less informative about the effectiveness of physiotherapy programmes that incorporate multiple treatment modalities, but are more likely to reflect physiotherapy as it is delivered in clinical practice. Only one included trial, Oerlemans 1999, took the pragmatic approach of testing a multimodal physiotherapy programme against a minimal treatment control group. Notably, this trial pre‐dates substantial developments in the pathophysiological models of CRPS and it is possible that a modern multimodal physiotherapy programme might differ substantially. In addition, the included trials rarely reported on adverse events (two out of 18 trials) and it is unclear whether or not this represents an absence of adverse events or a failure to report them.

While we categorised these interventions under the label "physiotherapy" in this Cochrane review, we recognise that rehabilitation therapies may be delivered by a range of different professionals, including occupational therapists and nurses.

Quality of the evidence

As reflected by the Grading of Recommendations Assessment, Development and Evaluation (GRADE) ratings, the overall quality of the evidence in this Cochrane review was low or very low. This reflects the fact that most included trials were at unclear or high risk of bias for criteria included under the standard domains of the Cochrane 'Risk of bias' tool, and under the additional 'Risk of bias' criteria of study size and duration included in this review. The included trials studied a broad heterogeneity of interventions, which afforded us limited opportunity to pool data and that, coupled with study size, led to issues of imprecision and inconsistency.

It is likely that small study effects, wherein there is a propensity for negative studies to not be published, might lead to an overly positive picture for some interventions, particularly in a field with such a limited evidence base. Evidence from the wider literature indicates that this might lead to an overly positive picture for some interventions (Dechartres 2013; Moore 2012; Nüesch 2010). In a review of meta‐analyses, Dechartres 2013 demonstrated that trials with fewer than 50 participants, which reflects most trials (17/18) included in this Cochrane review, returned effect estimates that were on average 48% larger than the largest trials and 23% larger than estimates from studies with sample sizes of more than 50 participants. We did not downgrade any of the GRADE judgements on the basis of publication bias, as there can be no direct evidence with so few trials for any given intervention. Moreover, it is accepted that existing approaches to detecting publication bias are unsatisfactory. To an extent our GRADE judgements reflect this risk through the assessment of imprecision and the limitations of included trials. Conversely, the issue of small study size with few included trials available for any single comparison raises the possibility of false negatives through lack of statistical power (Button 2013). Many of the comparisons we included in this review did not demonstrate a statistically significant difference. However, it is possible that we may have missed real effects on this basis.

The quality of reporting in many included trials was problematic. There was a lack of detailed descriptions of some interventions and a number of included trials did not present key numerical outcome data for all time‐points (9/18 trials) or insufficiently reported the scoring properties of their outcome measures for pain intensity (7/18 trials). The quality of reporting of pain‐related outcomes measures in clinical trials and observational studies is frequently insufficient (Smith 2015). In a systematic review of the quality of pain intensity reporting in three prominent pain journals, Smith 2015 found that nearly one quarter of published studies inadequately reported the type of pain intensity measure employed.

Potential biases in the review process

We conducted extensive and sensitive literature searches and included trials regardless of the language of publication. As such this Cochrane review probably represents the totality of currently available evidence. The choice to use the IMMPACT thresholds to determine the clinical importance of effect sizes is potentially controversial. What exactly constitutes an important difference on any given outcome measure remains contentious as the construct of a generic importance thresholds for a variety of interventions fails to reflect that patient satisfaction might differ substantially between interventions given their risks, costs and inconvenience, the point in the care pathway at which the participant arrives, and a range of other possible factors. Moreover, the IMMPACT thresholds are based on estimates of the degree of within‐person change from baseline that participants might consider to be clinically important, whereas the effect sizes focused on in this review reflect the average change between intervention‐groups following the interventions. For some pharmacological interventions the distribution of participant outcomes is bimodal (Moore 2013; Moore 2014a; Moore 2014b). That is, some participants experience a substantial reduction in symptoms, some minimal to no improvement and very few experience intermediate (moderate) improvements. In this instance, and if the distribution of participant outcomes reflects the distribution of treatment effects, then the average effect may be the effect that the fewest participants actually demonstrate (Moore 2013). It is therefore possible that a small average between‐group effect size might reflect that a proportion of participants responded very well to the intervention tested. The common solution to this problem is to conduct a ‘responder analysis’, which compares the proportion of participants achieving a clinically important improvement from baseline in the treatment and control groups. However responder analysis is very rare in rehabilitation therapies and there is no evidence to date to establish whether outcomes are commonly bimodal in rehabilitation trials. It therefore remains equally possible that a very small average between‐group effect might accurately represent the generally very small effects of an intervention for most or all individuals.

As such, the between‐group change is our sole available estimate of the specific effectiveness of the interventions in the included trials. Since the publication of our protocol for this review, Smart 2013, the OMERACT 12 group reported recommendations for minimally important difference for pain outcomes (Busse 2015). The group recommends a threshold of 10 mm on a 0 to 100 VAS as the threshold for minimal importance for average between‐group change, though stress that this should be interpreted with caution as it remains possible that estimates which fall closely below this point may still reflect a treatment that benefits an appreciable number of participants. Using this largely more lenient threshold would not alter our conclusions regarding clinical importance. The OMERACT thresholds present similar problems to those associated with all generic thresholds and it seems likely that the discussion around what constitutes clinical importance will continue. Arguably, the thresholds used in this Cochrane review of a 15% or 30% improvement in baseline levels of pain that are specifically attributable to the interventions do not represent unreasonably high thresholds.

Agreements and disagreements with other studies or reviews

The results of this systematic review are largely consistent with the conclusions drawn in our recent overview of systematic reviews of all interventions for CRPS (O'Connell 2013). In O'Connell 2013 we drew our conclusions mainly based on two non‐Cochrane reviews of physiotherapy interventions for CRPS (Daly 2009; Smith 2005) and we based the analysis of the evidence at the level of those included reviews. Our current review is more up‐to‐date, includes a number of additional studies and our conclusions are drawn from direct analysis of the original trials. Daly 2009 concluded that there was good to very good quality evidence to support the use of GMI for CRPS; and a review by Bowering 2013 (of which review author NEO was a co‐author) concluded that there was limited evidence to suggest that GMI may be effective for CRPS. In O'Connell 2013 we concluded that there was low quality evidence for the effectiveness of GMI. In this Cochrane review we downgraded the GRADE rating for the evidence related to GMI to very low, largely due to the inconsistency introduced by the inclusion of Schreuders 2014. In Schreuders 2014 the trial authors adjusted the treatment schedule compared to the schedules delivered by Moseley 2004 and Moseley 2006, though it was based on the same theoretical model. Smith 2005 concluded that there was some evidence that exercise, acupuncture, TENS, relaxation techniques, mirror therapy, GMI and combined treatment programmes may be helpful and that it was not possible to determine the effectiveness of individual treatments for CRPS‐I. Ten years on, that picture has not changed substantially. It is possible that future systematic reviews may provide further evaluations of the effectiveness of cortically‐directed sensory‐motor rehabilitation strategies (Plumbe 2013).

Recent clinical guidelines from the USA (Harden 2013) and the UK (Goebel 2012) have placed rehabilitation therapies as first‐line treatments for people with CRPS. Both guidelines describe and recommend an extensive range of possible physiotherapy modalities that might be employed. In making their recommendations, these guidelines (unlike this Cochrane review) draw on evidence from non‐randomised studies, expert consensus and studies of neuropathic pain generally. This Cochrane review highlights the fragility of the evidence underpinning these recommendations. The optimal approach to physiotherapy for people with CRPS and the true extent of potential benefits and risks remain uncertain. Also, there may be substantial redundancy within the broad range of therapies described or recommended in the guidelines.

Study flow diagram.
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Figure 1

Study flow diagram.

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'Risk of bias' graph: review authors' judgements about each 'Risk of bias' item presented as percentages across all included trials.
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Figure 2

'Risk of bias' graph: review authors' judgements about each 'Risk of bias' item presented as percentages across all included trials.

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'Risk of bias' summary: review authors' judgements about each 'Risk of bias' item for each included trial.
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Figure 3

'Risk of bias' summary: review authors' judgements about each 'Risk of bias' item for each included trial.

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Comparison 1 Graded motor imagery versus usual care, Outcome 1 Pain intensity (post‐treatment).
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Analysis 1.1

Comparison 1 Graded motor imagery versus usual care, Outcome 1 Pain intensity (post‐treatment).

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Comparison 1 Graded motor imagery versus usual care, Outcome 2 Function (0 to 10 patient specific functional scale) (post‐treatment).
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Analysis 1.2

Comparison 1 Graded motor imagery versus usual care, Outcome 2 Function (0 to 10 patient specific functional scale) (post‐treatment).

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Comparison 1. Graded motor imagery versus usual care

Outcome or subgroup title

No. of studies

No. of participants

Statistical method

Effect size

1 Pain intensity (post‐treatment) Show forest plot

2

49

Mean Difference (IV, Random, 95% CI)

‐14.45 [‐23.02, ‐5.87]

2 Function (0 to 10 patient specific functional scale) (post‐treatment) Show forest plot

2

49

Mean Difference (IV, Random, 95% CI)

1.87 [1.03, 2.71]
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Comparison 1. Graded motor imagery versus usual care
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