Description of the condition
Work-related upper limb disorder (WRULD), repetitive strain injury (RSI), cumulative trauma disorder (CTD), occupational overuse syndrome (OOS) and work-related complaints of the arm, neck or shoulder (CANS) are the most frequently used umbrella terms for disorders that develop as a result of repetitive movements, awkward postures and impact of external forces such as those associated with operating vibrating tools (Boocock 2009). Work-related complaints can be divided into specific conditions with relatively clear diagnostic criteria and pathology, such as carpal tunnel syndrome, and non-specific conditions, such as tension neck syndrome. These non-specific conditions are primarily defined by the locations of complaints, and their pathophysiology is less clearly defined or is relatively unknown (Staal 2007).
In the USA, cumulative trauma disorders account for between 56% and 65% of all occupational injuries (Melhorn 1998; Pilligan 2000). Overall, the estimated prevalence of work-related CANS is around 30% (Melhorn 1998), and several studies report a rapidly increasing incidence (Yassi 1997). Work-related CANS severely hampers the working population in Western countries. Approximately one-third of compensation costs in Australia and the USA are due to work-related CANS (Shanahan 2006; Staal 2007). As a result, these complaints are responsible for a considerable number of lost working days. The Labour Force Survey shows that an estimated 3.8 million working days (full-day equivalent) were lost in 2008-2009 in the UK because of musculoskeletal disorders mainly affecting the upper limbs or neck, caused or made worse by work. On average, each affected person took an estimated 17.5 days off in that 12-month period. This equates to an annual loss of 0.16 days per worker (HSE 2010).
The aetiology of CANS is considered to be multi-factorial. In most people, no specific diagnosis can be made (Armstrong 1993). In addition, no pathological, neurological or radiological characteristics can be found to support the diagnosis of 'non-specific' CANS (Staal 2007). Several personal and physical risk factors are found to be associated with CANS (Feleus 2007; Karels 2007; Roquelaure 2009), and increasing attention is being paid to its prevention and treatment (IJmker 2007; Shanahan 2006; Tulder 2007).
Description of the intervention
We defined conservative interventions as all interventions that are different from surgical interventions or injections. Types of conservative interventions that are prescribed or performed in the treatment of CANS include physiotherapy (exercises, mobilisation, electrotherapy and ultrasound), spinal manipulation, behavioural therapy and ergonomic measures or occupational therapy (e.g. working practices, splints). These interventions have in common that they are usually provided by general practitioners or physiotherapists, whereas the invasive interventions of surgery and injections require special skills and treatment facilities. Treatment may consist of a single intervention or of multiple interventions that may be provided by a member of a single discipline or members of several disciplines, as in multi-disciplinary treatment, whereby a team involving members of different disciplines such as physiotherapists, occupational therapists and psychologists provides treatment. Ergonomic measures used in the treatment of CANS include specially designed office furniture, computer keyboards and computer mice.
How the intervention might work
Conservative interventions, such as physiotherapy and ergonomic adjustments, play a major role in the treatment of CANS (Staal 2007; Tulder 2007). The working mechanism at tissue level of most interventions is unclear. Below we describe hypothesised mechanisms. The principal aims of these treatments are to decrease pain levels and improve function through methods such as muscle relaxation and re-education techniques, soft tissue mobilisation, cognitive interactions and workplace adjustments. Several exposures at the workplace are implied in the occupational origin of CANS, such as the use of too much force, too frequent (repetitive) movements and awkward positions. The aim of ergonomic and workplace adjustments is to influence these exposures by evaluating different sitting positions and making keyboard or mouse adjustments to prevent repetitive movements and awkward sitting postures. Physiotherapy interventions aim to (1) educate people about better sitting postures, (2) lower muscle intensity when working and (3) provide strengthening exercises to improve muscle condition and massage to relax muscles that are painful.
Why it is important to do this review
As shown above, work-related CANS is a common disorder that has considerable impact on many individuals and society as a whole and frequently results in work loss. There is thus an imperative to find the best ways of treating people with CANS, especially so that they can return to work. Two previous Cochrane reviews on this topic found insufficient evidence to permit firm conclusions on the effectiveness of frequently applied treatment strategies (Karjalainen 2000; Verhagen 2006). However, several new studies have been published during the past few years. Therefore, there is a need to determine whether new evidence has an impact on previous results and to identify the most effective treatment strategy. Do conservative interventions have a significant impact on short-term and long-term outcomes? This new review, which replaces the two above-mentioned reviews (Karjalainen 2000; Verhagen 2006), provides an update of the evidence on this topic.
To assess the effects of conservative interventions for work-related complaints of the arm, neck or shoulder (CANS) in adults on pain, function and work-related outcomes.
Criteria for considering studies for this review
Types of studies
We considered for inclusion in this review all randomised controlled trials (RCTs) and quasi-randomised controlled trials (using a method of allocating people to a treatment that is not strictly random, e.g. by date of birth or alternation). We also considered for inclusion cluster-RCTs, wherein the unit of randomisation is a group of individuals, and cross-over RCTs, in which participants, upon completion of one course of treatment, are switched to another.
Types of participants
We included studies that enrolled adults (18 years and older) suffering from work-related complaints of the arm, neck or shoulder (CANS). We excluded studies in which participants had acute trauma, neoplasms or inflammatory or neurological diseases. We considered complaints to be work-related when this was stated in the text, or when people were selected from a specific working population, such as an office, a factory or a laboratory.
Types of interventions
We considered all interventions that are not surgery or injections to be conservative interventions. We included all trials studying conservative interventions for the treatment of upper extremity work-related disorders in adults. Conservative interventions include exercises, relaxation, biopsychosocial rehabilitation programmes, physical applications such as ultrasound, biofeedback (a method of treatment that uses monitors to provide feedback to patients on physiological information of which they are normally unaware), myofeedback (a form of biofeedback that specifically focuses on muscular activity) and workplace adjustments. These interventions can be applied within or outside the workplace, in specialised training centres or in fitness centres. Treatment providers can vary but may involve clinical professionals such as physiotherapists, occupational therapists and psychologists or fitness instructors.
We included single conservative interventions or combinations of conservative interventions versus no intervention (e.g. waiting list control) or a placebo control, or a different conservative intervention. The studied intervention could be the only treatment or an add-on treatment. We excluded trials that tested injections and surgery.
We have set up separate comparisons for different categories of conservative interventions. We have grouped these primarily according to their working mechanisms as follows.
- Ergonomic workplace adjustments.
- Behavioural interventions.
- Other interventions.
Types of outcome measures
We included studies that used the following primary outcome measures.
- Ability to work (e.g. sickness absence (days off work), return to work, productivity loss at work, change of occupation).
- Global perceived effect (e.g. overall improvement) (Beurskens 1996).
- Healthcare consumption (e.g. physician consultations, physiotherapy, ergonomic adjustments, intake of analgesics).
- Recurrence of injury, disorder or complaint.
Search methods for identification of studies
For this updated version of our review, we searched the Cochrane Central Register of Controlled Trials (The Cochrane Library, 31 May 2013), MEDLINE (1950 to 31 May 2013), EMBASE (1988 to 31 May 2013), CINAHL (1982 to 31 May 2013), AMED (1985 to 31 May 2013), PsycINFO (1806 to 31 May 2013), PEDro (the Physiotherapy Evidence Database; inception to 31 May 2013) and OTseeker (the Occupational Therapy Systematic Evaluation of Evidence Database; inception to 31 May 2013). We did not apply any language restrictions.
In MEDLINE, we combined the subject-specific strategy with the sensitivity- and precision-maximising version of the Cochrane Highly Sensitive Search Strategy (Lefebvre 2009) for identifying randomised trials in MEDLINE and modified for use in other databases. Search strategies for the Cochrane Central Register of Controlled Trials, MEDLINE and EMBASE are shown in Appendix 1.
Searching other resources
We also searched reference lists of included articles and contacted experts in the field.
Data collection and analysis
Selection of studies
Three review authors (SMS, BWK and SMAB-Z) independently selected trials by inspecting titles, keywords and abstracts to determine whether studies met the inclusion criteria regarding design, participants and interventions. Full publications of studies of any possible relevance were retrieved for final assessment. Next, the review authors independently performed a final selection of the trials to be included in the review using a standardised form. Disagreements were resolved by consensus and, if necessary, by fourth party adjudication (APV).
Data extraction and management
Two review authors (SMAB-Z and APV) independently extracted data on trial methods, participants, settings, interventions, care providers, types of outcome measures, duration of follow-up, loss to follow-up and results using a standardised data extraction form from Verhagen 2006. Disagreements were resolved by consensus and, if necessary, by third party adjudication (HCWdV).
Assessment of risk of bias in included studies
Two review authors (BWK and SMS) independently assessed the risk of bias using a modified version of the assessment tool developed by The Cochrane Collaboration (Furlan 2009; Higgins 2011) ( Table 1). This tool incorporates the Delphi list (Verhagen 1998), as used in previous versions of this review, and involves assessment of randomisation (sequence generation and allocation concealment), blinding (of participants, care providers and outcome assessors), completeness of outcome data, selection of outcomes reported and four other sources of bias. Disagreement was resolved by consensus or, if disagreement persisted, a third review author (APV) made the final decision.
We derived the interobserver reliability of the risk of bias assessment by Kappa statistics. We considered Kappa values > 0.7 as showing good agreement, between 0.5 and 0.7 moderate agreement and < 0.5 poor agreement.
Measures of treatment effect
We presented the various outcome measures separately. For dichotomous data, we expressed results, if possible, as risk ratios (RRs) with corresponding 95% confidence intervals (95% CIs). For continuous data, we calculated mean differences or, when outcome measures were dissimilar, standardised mean differences (SMDs) with 95% confidence intervals (Lau 1997).
Unit of analysis issues
Most treatment was targeted to individuals. However, in some trials, treatment allocation was randomised by groups or clusters rather than individuals.
For cluster-randomised trials that did not adjust for the cluster effect, we calculated the design effect based on the number of clusters and the number of participants and an assumed intraclass correlation (ICC) of 0.1 (Campbell 2001), as indicated in the Cochrane Handbook for Systematic Reviews of Interventions; Higgins 2011). We then used this design effect to adjust the number of participants included in the analysis.
When sufficient studies were available, we conducted a sensitivity analysis.
For cross-over trials, we did not know what a suitable wash-out period would be for the interventions of interest. Therefore, to avoid the carry-over of the treatment from the first period, we restricted the analysis to the first period of the trial only. This was possible for two studies (Sjögren 2005; Ylinen 2007). One other study (Takala 1994) did not provide enough data for this analysis and we included this study as if it were a parallel group trial. We accept that this may have resulted in the underestimation of the treatment effect. The fourth cross-over trial (Ferguson 1976) did not provide enough data to be included in the analysis.
Dealing with missing data
For dichotomous data, we performed an intention-to-treat analysis whereby all missing people were considered to have a bad outcome. However, for continuous data, when dropouts were identified, we used the actual number of participants contributing data at the relevant outcome assessment. Furthermore, we refrained from imputing values for standard deviations unless missing standard deviations could be derived from confidence intervals, standard errors or presented P values in the same study.
Assessment of heterogeneity
Clinicians on the review team assessed clinical heterogeneity on the basis of information on the study population (chronic vs. acute, specific vs non-specific), interventions (exercises, massage, ergonomic interventions, etc.), control interventions (no treatment vs. active treatment), outcomes (pain, function, recovery and sick leave) and timing of follow-up (short term: less than three months; long term: six months or longer). We assessed statistical heterogeneity between pooled trials using a combination of visual inspection of the graphs and consideration of the I
Assessment of reporting biases
We assessed publication bias by using a funnel plot.
We used Review Manager (RevMan 2011) to analyse the data. We pooled studies that we judged to be similar with regard to participants, interventions, comparisons and outcomes.
The quality of the evidence for a specific outcome was based upon five domains and was downgraded by one level for each of the following factors if encountered.
- Limitations in design (> 25% of participants came from studies with high risk of bias).
- Inconsistency of results (significant statistical heterogeneity (I
2> 40%) or inconsistent findings among studies (≤ 75% of participants report findings in the same direction)).
- Indirectness (i.e. generalisability of findings).
- Imprecision (total number of participants < 300 for each outcome).
- Other (e.g. publication bias, flawed design).
Two review authors (SMS, BWK) independently judged the quality of evidence for each outcome using these five factors. We considered single randomised studies (n < 300) to be inconsistent and imprecise and to provide "low quality evidence", which could be further downgraded to "very low quality evidence" if there were also limitations in design (i.e. high risk of bias), indirectness or other considerations. We rated the quality of the evidence as high, moderate, low or very low with the following implications.
- High quality: Further research is very unlikely to change our confidence in the estimate of effect. Data are sufficient with narrow confidence intervals. No reporting biases are known or suspected; all domains were fulfilled.
- Moderate quality: Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate; one of the domains was not fulfilled.
- Low quality: Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change it; two of the domains were not fulfilled.
- Very low quality: Great uncertainty surrounds the estimate; three of the domains were not fulfilled.
Subgroup analysis and investigation of heterogeneity
We performed subgroup analyses to evaluate the effects of specific work-related CANS (e.g. a specific cause and diagnosis are established) versus non-specific work-related CANS, setting of treatment (work vs. outside work location), care provider (general practitioner, physiotherapist or occupational therapist), location of the complaint (neck/shoulder vs. arm) or duration of the complaint (chronic vs. (sub)acute).
We performed sensitivity analyses by pooling only results from studies that we considered to have a low risk of bias.
Description of studies
Results of the search
We randomly allocated two out of four of the review authors (SMAB-Z, SMS, BWK and APV) to perform the systematic search process independently. This resulted in 4,945 references after duplicates were removed. Based on title and abstract, we selected 275 references for full-text retrieval. Of these, we finally selected 44 studies (62 publications) for inclusion in this review (Figure 1).
|Figure 1. Study flow diagram.|
Of the 44 included studies, 35 studies randomly assigned participants individually to intervention or control groups. Two studies performed group randomisation (Heuvel 2003; Waling 2000), and three studies used cluster-randomisation (Andersen 2008a; Andersen 2008b; Esmaeilzadeh 2012). Three studies used a cross-over design (Ferguson 1976; Takala 1994; Ylinen 2007), and one study used a cross-over design with cluster-randomisation (Sjögren 2005). We adjusted the study outcome data for an assumed cluster effect for Heuvel 2003 and Andersen 2008b. We did not do so for Sjögren 2005 because this study used both a cluster-randomised and a cross-over design. For this study, we assumed that the too conservative estimate for the cross-over design would balance the too narrow confidence intervals resulting from the cluster design. Equally, we did not adjust the data for Waling 2000 or Esmaeilzadeh 2012 because groups were clustered only on the basis of the most convenient timing for participants. We assumed that the cluster effect would be negligible here. Andersen 2008a did not provide data for meta-analysis; therefore, we could not adjust study outcomes here. We excluded Ferguson 1976 from the analysis because these investigators did not present data from the first phase of the cross-over trial.
One study (Abasolo 2005) was extremely large; researchers included 13 077 participants, of which 1,605 suffered from work-related neck pain. In all other studies, the number of participants in each treatment group varied from nine to 187 (mean 108.4). In 19 of the other 43 studies, the smallest intervention group had fewer than 25 participants.
Of the 44 studies, 18 originated from the Scandinavian countries (eight from Finland alone); eight from the rest of Europe (of which five are from The Netherlands); 14 from the USA, Canada and Australia; ; two from China and two from Turkey.
In total, we included in this review data from 6,580 participants. Thirty-three studies selected study populations such as industrial workers or hospital staff.
Thirty-six studies included people with non-specific neck and shoulder complaints or non-specific upper extremity disorders. Three studies included people with work-related carpal tunnel syndrome (Rempel 1999; Tittiranonda 1999; Werner 2005) and two rotator cuff tendinitis (Cheng 2007; Szcurko 2009), whereas shoulder impingement (Bang 2000), epicondylitis (Nourbakhsh 2008) and hand or wrist complaints (Stralka 1998) were included in one study each.
A total of 39 studies included people with chronic complaints varying in duration between three and 12 months. When people with 'prevalent complaints' were included, the mean duration of the complaints at baseline appeared to vary between three months and 11 years. Four studies involved people with recent (< six weeks) onset of complaints (Heuvel 2003; Ketola 2002; Moore 1996; Tittiranonda 1999).
Sixteen studies included only women, and one study included men only (Ferguson 1976); all other 27 studies included both men and women.
We evaluated the definition of 'work-relatedness' in all studies. Most studies (n = 36) stated that work-relatedness was due to including office or computer workers with musculoskeletal complaints or complaints caused by the work or by repetitive stress. Authors used statements such as "...reported a gradual onset of symptoms that were apparently work-related", "...reported pain or complaints during work tasks", "...performed data processing tasks for 8 hours a day" or "...pain due to repetitive use or prolonged static postures".
Thirty-nine studies used pain as an outcome measure, most often using a visual analogue scale (VAS) or a numerical rating scale (NRS). Eight studies used an index or composite score measure 'pain complaints', 12 studies used 'return to work' or 'sick leave' as an outcome measure and seven studies measured recovery, benefit or satisfaction. Other outcome measures included disability (by questionnaire) or strength (by dynamometer). We defined short-term outcomes as outcomes measured within three months after randomisation, and long-term outcomes as those measured more than three months after randomisation.
The 44 included studies evaluated seven different types of interventions. Twenty-five studies employed only two study arms, 14 studies had three and five studies used altogether four study arms. No studies compared a conservative treatment option versus other treatments such as oral medication, injection or surgery. Twenty-nine studies included a control intervention such as placebo treatment (four studies: Goldman 2010; Nourbakhsh 2008 Stralka 1998; Tittiranonda 1999), no treatment controls (13 studies: Dellve 2011; Esmaeilzadeh 2012; Heuvel 2003; Kamwendo 1991; Ketola 2002; Lundblad 1999; Ma 2011; Marangoni 2010; Rempel 2007; Sandsjö 2010; Sjögren 2005; Takala 1994; Viljanen 2003), a waiting list control group (four studies: Bru 1994; Moore 1996; Spence 1989; Spence 1995), a counselling or discussion control group (three studies: Andersen 2008a; Andersen 2008b; Waling 2000) or usual care controls (four studies: Abasolo 2005; Bernaards 2006; Martimo 2010; Meijer 2006).
One study did not evaluate a specific treatment but rather assessed treatment delivered by rheumatologist versus general practitioner (Abasolo 2005). All other interventions can be grouped as follows.
Twenty-one studies evaluated a form of exercise therapy including specific forms of exercises such as proprioceptive neuromuscular facilitation (PNF) (Ferguson 1976), Feldenkrais therapy (Lundblad 1999) or Mensendieck training (van Eijsden 2008). All 21 studies included participants with non-specific neck and shoulder pain, except for one study, which included participants with rotator cuff tendinitis (Szcurko 2009).
Exercises were compared with a control group of no treatment or an intervention like counselling in 11 studies (Andersen 2008a; Andersen 2008b; Dellve 2011; Kamwendo 1991; Lundblad 1999; Ma 2011; Sjögren 2005; Takala 1994; Viljanen 2003; Waling 2000; Ylinen 2003), with other exercises in eight studies (Andersen 2008a; Andersen 2008b;Ferguson 1976; Hagberg 2000; Lundblad 1999; van Eijsden 2008; Waling 2000; Ylinen 2003), with behavioural therapy in three studies (Dellve 2011; Ma 2011; Viljanen 2003), with massage in two studies (Ferguson 1976; Levoska 1993) and with manual therapy (Ylinen 2007) and neuropathic care (Szcurko 2009) in one study each. Exercise was evaluated as an add-on treatment to ergonomic instructions in two studies (Bernaards 2006; Omer 2003) and in addition to breaks during computer work in one study (Heuvel 2003). One study (Vasseljen 1995) compared physical therapy provided individually with group physical therapy, with both including exercises given at the workplace.
Various ergonomic strategies were evaluated in 13 studies and can be regarded as two different strategies: work hardening strategies (Bernaards 2006; Cheng 2007; Ketola 2002; Lundblad 1999) and strategies related to workplace computer or keyboard use (Esmaeilzadeh 2012; Heuvel 2003; Kamwendo 1991; Marangoni 2010; Martimo 2010; Rempel 1999; Rempel 2007; Ripat 2006; Tittiranonda 1999). Three studies included participants with specific complaints such as rotator cuff tendinitis (Cheng 2007) or carpal tunnel syndrome (Rempel 1999; Tittiranonda 1999).
Eight studies compared ergonomic programmes versus a no treatment control group (Bernaards 2006; Esmaeilzadeh 2012; Heuvel 2003; Ketola 2002; Lundblad 1999; Marangoni 2010; Martimo 2010; Rempel 2007) and one versus placebo (Tittiranonda 1999). Five studies compared various ergonomic interventions versus each other (Ketola 2002; Marangoni 2010; Rempel 1999; Rempel 2007; Ripat 2006), and in two studies, ergonomic changes at the workplace were an add-on treatment to exercises (Cheng 2007; Kamwendo 1991). One study compared both intensive ergonomic guidance and education in ergonomics (Ketola 2002) and an ergonomic programme versus an exercise group (Lundblad 1999).
3. Behavioural treatment
Nine studies evaluated a form of behavioural strategy, all in participants with non-specific neck and shoulder pain (Bru 1994; Dellve 2011; Ma 2011; Moore 1996; Sandsjö 2010; Spence 1989; Spence 1995; Viljanen 2003; Voerman 2007). One other study evaluated a multi-disciplinary treatment, including physical exercises and relaxation treatment, compared with usual care (Meijer 2006).
Four studies compared relaxation therapy, cognitive strategies or bio/myofeedback versus a waiting list control (Bru 1994; Moore 1996; Spence 1989; Spence 1995), two studies used a no-treatment control group (Dellve 2011; Ma 2011) and another two studies compared with usual care (Sandsjö 2010; Viljanen 2003). One study evaluated a behavioural strategy as an add-on treatment to ergonomic counselling (Voerman 2007).
Three studies evaluated massage as a part of the treatment compared with exercises in two studies (Ferguson 1976; Levoska 1993) and with additional treatment to spinal manipulative therapy in one study (Leboeuf 1987).
5. Electrical therapy
Two studies evaluated a splint. One study compared an energised splint versus placebo in participants with hand and wrist problems (Stralka 1998), and another study evaluated the use of a splint as add-on treatment to video education in participants with carpal tunnel syndrome (Werner 2005). One study evaluated low-frequency electrical stimulation versus placebo in participants with epicondylitis (Nourbakhsh 2008).
6. Manual therapy
Two studies evaluated a form of manual therapy (Bang 2000; Ylinen 2007). One study compared manual therapy versus exercises (Ylinen 2007), and another study evaluated manual therapy as an additional treatment to exercise in participants with shoulder impingement syndrome (Bang 2000).
One study compared amitriptyline, that is, pain medication, versus placebo in participants with non-specific neck and shoulder pain (Goldman 2010).
Most of the excluded studies did not differentiate between participants with a musculoskeletal disorder and those without. They included healthy workers, as well as workers with neck pain, without separate reporting of results. This means that both prevention and treatment were evaluated in the studies (Figure 1).
Risk of bias in included studies
|Figure 2. Risk of bias summary: review authors' judgements about each risk of bias item for each included study.|
Initially, there was agreement between both review authors of 83.5% (Kappa = 0.64), meaning a moderate level of agreement. The third review author made the final decision for 16 items.
Overall the amount of non-information (i.e. items that scored unclear risk of bias) varied between 11.4% (dropout rate described) and 97.7% (selective outcome reporting). The items that scored high on risk of bias were intention-to-treat analysis (52.3%), dropout rate described and adequate (27.3%), non-blinded participants (34.1%) and caregivers (34.1%) and outcome assessment (34.1%). See Figure 3.
|Figure 3. Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.|
Based on our criterion of low risk of bias, "an overall sum score 50 per cent or more of the maximum score", nine studies could be categorised as having low risk of bias (Meijer 2006; Nourbakhsh 2008; Rempel 1999; Stralka 1998; Szcurko 2009; Tittiranonda 1999; van Eijsden 2008; Viljanen 2003; Ylinen 2003). We consider these studies to have low risk of bias in our GRADE analysis, meaning that they do not downgrade the level of evidence because of the design.
Twenty-two studies provided no information on the randomisation procedure (Figure 2). We judged four studies to have an inadequate randomisation procedure (item 1) (Ferguson 1976; Marangoni 2010; Sandsjö 2010; Werner 2005).
We judged 11 studies to have described an adequate procedure for concealing allocation (item 2) (Bernaards 2006; Esmaeilzadeh 2012; Goldman 2010; Hagberg 2000; Meijer 2006; Sjögren 2005; Szcurko 2009; Tittiranonda 1999; van Eijsden 2008; Viljanen 2003; Ylinen 2003) and judged five studies to have done it inadequately (Marangoni 2010; Martimo 2010; Nourbakhsh 2008; Ripat 2006; Stralka 1998). The remaining 28 studies did not describe how or whether they concealed their randomisation procedure.
Eight studies described blinding of outcome assessment (Bang 2000; Ferguson 1976; Goldman 2010; Nourbakhsh 2008; Rempel 1999; Stralka 1998; Tittiranonda 1999; Viljanen 2003), in six studies participants were blinded (Goldman 2010; Nourbakhsh 2008; Rempel 1999; Stralka 1998; Tittiranonda 1999; Viljanen 2003) and in four studies the care provider was blinded (Goldman 2010; Rempel 1999; Stralka 1998; Tittiranonda 1999).
Incomplete outcome data
We judged 23 (52.3%) of the included studies to have a high risk of bias, as they clearly did not perform an intention-to-treat (ITT) analysis. Only 14 (32.5%) of the included studies performed an ITT analysis or presented complete data. The dropout rate was described and acceptable, that is, was less than 20%, in 26 (59.1%) of the studies.
We could retrieve a study protocol for only one study (van Eijsden 2008). Hence this was the only study that we scored as having a low risk of bias due to selective outcome presentation. We judged all remaining studies to have an unclear risk of bias due to selective reporting.
Other potential sources of bias
We assessed four other sources of bias: baseline imbalance, whether co-interventions were avoided or similar, whether compliance was acceptable and whether timing was comparable. We judged 29 studies (65.9%) to have a low risk of bias as the result of no baseline imbalance, although in nine studies, baseline similarity was unclear.
Only five studies reported that co-interventions were avoided or similar (Ma 2011; Nourbakhsh 2008; Sandsjö 2010; Viljanen 2003; Ylinen 2003), and two were considered to have a high risk of bias concerning co-interventions (Andersen 2008b; Szcurko 2009). Seventeen studies reported acceptable compliance rates. Thirty-seven studies reported comparable timing of outcome assessment. Only one study (Werner 2005) clearly reported that the 12-month outcome assessment varied between seven and 15 months.
Effects of interventions
In total, 29 studies presented dichotomous data or point estimates and measures of variability for their primary outcomes. According to our judgement, studies overall had low power and high risk of bias. Therefore the quality of evidence varied between low and very low.
Exercise versus no treatment controls
Ten studies presented short-term results on pain. Overall we found that exercise did not reduce pain when compared with no treatment or discussion controls, or when given as additional treatment ( Analysis 1.1). Five studies (Dellve 2011; Ma 2011; Sjögren 2005; Takala 1994; Viljanen 2003) compared exercise versus no treatment and found no difference in pain (SMD -0.52, 95% CI -1.08 to 0.03). All studies concerned participants with chronic non-specific complaints.
In a sensitivity analysis, we omitted all studies that we judged to have a high risk of bias (Dellve 2011; Ma 2011; Sjögren 2005; Takala 1994) and still found no differences between groups. According to four studies (Andersen 2008a; Andersen 2008b; Szcurko 2009; Waling 2000), exercise did not reduce pain any more than participating in a discussion group.
In a subgroup analysis of participants with specific complaints, one study (Szcurko 2009), which was the only study judged to have a low risk of bias, showed that participation in a discussion control group reduced pain more than exercise (mean difference (MD) 0.74, 95% CI 0.30 to 1.18). We found no differences in pain in the subgroup of chronic non-specific complaints.
Two studies (Bernaards 2006; Omer 2003) compared exercise as an addition to work style education versus education alone and found conflicting results: One study (Omer 2003) reported significant benefit associated with additional exercises, and the other study (Bernaards 2006) found no differences.
Overall, this comparison suffered from major heterogeneity (I
We conclude that for pain, very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) that exercises lead to similar levels of pain as no treatment at both short-term and long-term follow-up.
We also assessed publication bias for this comparison. The funnel plot (Figure 4) shows that small studies with negative effects are missing in the right lower quadrant, which indicates possible publication bias.
|Figure 4. Funnel plot of comparison: 1 Exercise versus no treatment controls, outcome: 1.1 Pain intensity, short term.|
Exercise versus active treatment controls
According to four studies (Andersen 2008b; van Eijsden 2008; Vasseljen 1995; Waling 2000), overall regular exercises reduce pain in the short term more than specific exercises (SMD 0.45, 95% CI 0.14 to 0.75) ( Analysis 2.1). All four studies included participants with chronic non-specific complaints.
In a sensitivity analysis from which we omitted the studies we judged to have a high risk of bias (Andersen 2008b; Vasseljen 1995; Waling 2000), results showed that regular exercises reduce pain more than specific exercises. According to two studies (van Eijsden 2008; Ylinen 2003), both with a low risk of bias, regular exercise leads to less pain in the short term than specific exercises (MD 0.80, 95% CI 0.09 to 1.51) (van Eijsden 2008) but not in the long term (pooled SMD 0.10, 95% CI -0.18 to 0.38). One study (Ylinen 2007) compared exercises versus manual therapy and found no difference in short-term pain (MD 0.00, 95% CI -9.63 to 9.63).
We conclude that for pain, low-quality evidence (downgraded by limitations of design and imprecision) suggests a benefit of regular exercises over specific exercises at short-term follow-up only.
Ergonomic intervention versus no treatment controls
Five studies (Bernaards 2006; Cheng 2007; Ketola 2002; Martimo 2010; Tittiranonda 1999) compared ergonomic interventions versus placebo or no treatment or as an additional treatment for short-term pain ( Analysis 3.1). One study (Tittiranonda 1999) evaluated various keyboards versus placebo in participants with carpal tunnel syndrome (CTS) and found a reduction in pain with the placebo keyboard (SMD 0.53, 95% CI 0.01 to 1.04). Three studies (Bernaards 2006; Ketola 2002; Martimo 2010) compared ergonomic interventions versus no treatment in participants with non-specific complaints and found no differences between the groups (SMD -0.07, 95% CI -0.36 to 0.22), although this analysis suffered from moderate heterogeneity (I
Subgroup analysis of the study by Ketola 2002 involving subacute participants only showed pain to decrease more with ergonomic interventions than with no treatment (SMD -0.52, 95% CI -0.99 to -0.05), while the two studies with chronic complaints (Bernaards 2006; Martimo 2010) reported no difference (SMD 0.10, 95% CI -0.09 to 0.29).
Four studies (Bernaards 2006; Esmaeilzadeh 2012; Ketola 2002; Lundblad 1999) compared ergonomic interventions versus no treatment in reducing pain over the long term and found a significant difference in favour of the ergonomic intervention (SMD -0.76, 95% CI -1.35 to -0.16). However, this analysis ( Analysis 3.2) exhibited large heterogeneity (I
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) indicates that ergonomic interventions lead to similar results as no treatment in reducing pain in the short term. For the long term, very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows a small benefit of ergonomic interventions when compared with no treatment.
In subgroups of subacute participants and in the subgroup of participants with specific complaints, we found a very low level of evidence (downgraded by limitations of design, imprecision and inconsistency) for ergonomic interventions reducing pain more than placebo, or when given as additional interventions to exercises.
Ergonomic intervention versus active treatment controls
One study (Rempel 1999) evaluated an experimental keyboard versus the standard one for reducing pain in the short term in participants with CTS. Another study (Tittiranonda 1999) evaluated three different keyboards versus placebo, also for reducing pain in the short term. One study (Ketola 2002) evaluated both short-term and long-term pain reduction with intensive versus standard ergonomic training in participants with recent non-specific complaints, and another study evaluated reduction in pain over the long term due to ergonomic interventions versus regular exercises in participants with chronic non-specific complaints (Lundblad 1999). Overall, we found no differences in pain between the groups in the short term (SMD 0.11, 95% CI -0.24 to 0.46) ( Analysis 4.1) or over the long term (SMD -0.02, 95% CI -1.22 to 1.18) ( Analysis 4.2).
We found very low-quality evidence overall (downgraded by limitations of design, imprecision and inconsistency) showing that various ergonomic interventions lead to similar pain levels in the short term and over the long term.
Behavioural intervention versus no treatment controls
Four studies (Dellve 2011; Ma 2011; Sandsjö 2010; Viljanen 2003) evaluated a behavioural intervention versus no treatment and found no difference in pain (SMD -0.67, 95% CI -1.49 to 0.16) ( Analysis 5.1; Analysis 5.2). Three studies (Moore 1996; Spence 1989; Spence 1995) compared a behavioural intervention versus a waiting list control group, all including participants with chronic non-specific complaints, and found that the intervention reduced pain in the short term (SMD -0.74, 95% CI -1.32 to -0.15).
In a sensitivity analysis we omitted the studies we judged to have a high or unclear risk of bias and only one remained (Viljanen 2003). This study reported no difference in pain intensity in the short term (SMD 0.08, 95% CI -0.16 to 0.33) or over the long term (SMD -0.04, 95% CI -0.28 to 0.20).
Meta-analyses of behavioural interventions versus no treatment or a waiting list control suffered from moderate to large heterogeneity (I
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) indicates that behavioural intervention leads to similar pain levels at short term and over the long term as no treatment.
Behavioural intervention versus active treatment controls
Two studies (Spence 1989; Spence 1995) evaluated various behavioural interventions versus regular treatment and found no differences between the groups in terms of pain (SMD -0.23, 95% CI -0.73 to 0.27) ( Analysis 6.1; Analysis 6.4). We judged all three studies to have a high risk of bias, and all included participants with chronic non-specific complaints. Three studies (Dellve 2011; Ma 2011; Viljanen 2003) evaluated behavioural interventions versus exercises and found no differences in pain in the short term (SMD -0.02, 95% CI -0.24 to 0.19). Sensitivity analysis on the one study with low risk of bias (Viljanen 2003) also found no differences between groups in the short term (SMD 0.00, 95% CI -0.24 to 0.24) or over the long term (SMD 0.08, 95% CI -0.16 to 0.32).
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) indicates that various behavioural interventions lead to similar results in reducing pain in the short term and over the long term.
Exercise versus no treatment controls
Three studies (Ma 2011; Lundblad 1999; Viljanen 2003) evaluated exercise versus no treatment. When we pooled study results, we found no differences in disability between study groups at short-term (SMD -0.77, 95% CI -2.50 to 0.97) or long-term follow-up (SMD 0.14, 95% CI -0.08 to 0.34; Analysis 1.3; Analysis 1.4; Analysis 1.5).
Exercise was compared with discussion in two studies (Szcurko 2009; Ylinen 2003). Szcurko 2009 found that discussion relieved disability better than exercise in the short term (SMD 0.51, 95% CI 0.08 to 0.94), whereas exercise produced better results in the long term in the study by Ylinen 2003 (SMD -0.55, 95% CI -0.87 to -0.23; Analysis 1.3; Analysis 1.5). Heterogeneity varied between 0 and 93%, and we could explain this by risk of bias or subgroups.
One study (Bernaards 2006), which we judged to have a high risk of bias, compared exercises only with exercises in addition to work style education. This study found no differences in disability (risk ratio (RR) 1.00, 95% CI 0.82 to 1.21; Analysis 1.4).
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) indicates that exercises lead to similar levels of disability as no treatment both in the short term and over the long term.
Exercise versus active treatment controls
One study each compared the effects of different types of exercise (van Eijsden 2008) and exercise with manual therapy (Ylinen 2007) on disability in the short term. Neither study found a significant difference in disability in the short term: van Eijsden 2008—MD 2.00, 95% CI -2.18 to 6.18; Ylinen 2007—MD 1.00, 95% CI -2.20 to 4.20; Analysis 2.3.
Two studies compared the effects of different types of exercise (van Eijsden 2008; Ylinen 2003) on disability in the long term. No difference in disability was noted between exercises and other exercises in the long term in these two studies (SMD 0.11, 95% CI -0.17 to 0.38; Analysis 2.4).
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows that exercises lead to similar levels of disability as other exercises or manual therapy both in the short term and over the long term.
Ergonomic intervention versus no treatment controls
One study (Tittiranonda 1999) evaluated various keyboards versus placebo in participants with carpal tunnel syndrome (CTS) and found that participants using the placebo keyboard felt less disabled (MD 0.93, 95% CI 0.28 to 1.57; Analysis 3.3).
Three studies (Bernaards 2006; Esmaeilzadeh 2012; Lundblad 1999) evaluated ergonomic interventions in chronic non-specific participants versus no treatment and found no differences in disability at long-term follow-up (RR 0.98, 95% CI 0.85 to 1.14; SMD -0.33, 95% CI -0.71 to 0.06; Analysis 3.4; Analysis 3.5).
One study (Cheng 2007) found that ergonomic interventions and exercise decreased disability more than exercise alone in participants with rotator cuff pain (MD -9.00, 95% CI -15.02 to -2.98).
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows that ergonomic interventions lead to similar levels of disability as no treatment both in the short term and over the long term.
Behavioural intervention versus no treatment controls
Two studies (Ma 2011; Viljanen 2003) compared behavioural interventions versus no treatment in reducing disability in the short term. Pooling their results led to such a large degree of heterogeneity (I
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows that in the short term behavioural interventions lead to similar levels of disability as no treatment. Furthermore, we conclude that very-low quality evidence (downgraded by limitations of design, imprecision and inconsistency) suggests that behavioural interventions decrease disability in the short term more than being in a waiting list control group.
Behavioural intervention versus active treatment controls
Three studies (Ma 2011; Dellve 2011; Viljanen 2003) compared behavioural interventions and exercises in reducing disability or, conversely, in improving work ability in the short term. There was no difference between the groups in disability (SMD -0.57, 95% CI -1.66 to 0.52; Analysis 6.2) or in work ability (SMD -0.15, 95% CI -0.84 to 0.54; Analysis 6.3). One study (Viljanen 2003) also measured long-term effects on disability and work ability and found no differences between behavioural interventions and exercises: disability—MD 0.00, 95% CI -3.65 to 3.65; Analysis 6.5; work ability—MD 0.20, 95% CI -0.09 to 0.49; Analysis 6.6.
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows that in the short term behavioural interventions lead to similar levels of disability as exercises.
Exercise versus no treatment controls
Three studies, all with participants with chronic non-specific complaints (Bernaards 2006; Heuvel 2003; Waling 2000), compared exercise with no treatment (Waling 2000) versus exercise additional to work style education (Bernaards 2006) and with computer breaks (Heuvel 2003) on short-term recovery. We pooled the results of three different exercise interventions compared with no treatment in Waling 2000 and found that exercise improves recovery (RR 0.53, 95% CI 0.37 to 0.78; Analysis 1.6). In contrast, exercises conducted as additional treatment did not seem to improve recovery more than regular exercise in the two studies by Bernaards 2006 and Heuvel 2003 (RR 1.25, 95% CI 0.18 to 1.93; Analysis 1.7). We judged all three studies to have a high risk of bias. Ferguson 1976 did not find a significant effect on recovery, but the study could not be included in the meta-analysis.
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) suggests that in the short term exercises improve recovery more than no treatment, but there is no additional benefit on recovery if exercises are administered together with computer breaks or work style education.
Exercise versus active treatment controls
Three studies (van Eijsden 2008; Vasseljen 1995; Waling 2000) compared the effects of different types of exercise on recovery in the short term. One study (Levoska 1993) compared the recovery-improving effects of exercise and massage, and another study (Ylinen 2007) compared exercise with manual therapy. There were no differences in effectiveness between different forms of exercise (RR 0.86, 95% CI 0.43 to 1.71; Analysis 2.5) or between exercises and massage (RR 0.78, 95% CI 0.55 to 1.11). Only manual therapy appeared to improve recovery more than exercises in one study (Ylinen 2007), which we judged to have a high risk of bias (RR 1.88, 95% CI 1.29 to 2.74; Analysis 2.5).
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows no differences between different forms of exercise or between exercise and massage in recovery in the short term. Manual therapy may be more effective than exercise based on only one study with a high risk of bias.
Ergonomic intervention versus no treatment controls
One study (Tittiranonda 1999) compared the effects of different keyboards on recovery in the short term in participants with carpal tunnel syndrome (CTS). Recovery was better with participants who used a placebo keyboard (RR 1.89, 95% CI 0.85 to 4.21; Analysis 3.7). Another study (Bernaards 2006) compared an ergonomic intervention with no treatment in participants with chronic non-specific complaints. Participants recovered better in the ergonomic intervention group when measured at short-term (RR 0.88, 95% CI 0.78 to 0.99; Analysis 3.7) and at long-term follow-up (RR 0.90, 95% CI 0.81 to 1.00; Analysis 3.8).
We conclude that very low-quality evidence (downgraded by limitations of design, imprecision and inconsistency) shows that both in the short term and over the long term ergonomic interventions improve recovery more than no treatment.
Exercise versus no treatment controls
Two studies (Lundblad 1999; Viljanen 2003) evaluated the effects of exercise versus no treatment on sick leave in the long term. We found no differences between groups (SMD -0.03, 95% CI -0.26 to 0.19; Analysis 1.8). We judged one of the two studies (Viljanen 2003) to have a low risk of bias.
We conclude that moderate-quality evidence (downgraded by imprecision) shows no difference between exercise and no treatment on sick leave over the long term.
Ergonomic intervention versus no treatment controls
Two studies (Heuvel 2003; Martimo 2010) compared the effects of ergonomic interventions and no treatment on sick leave at short term and found no difference (RR 0.49, 95% CI 0.32 to 0.76; Analysis 3.9).
We conclude that low-quality evidence (downgraded by limitations of design and imprecision) shows that in the short term ergonomic interventions lead to similar effects on sick leave as no treatment.
Behavioural intervention versus no treatment controls
Three studies (Dellve 2011; Sandsjö 2010; Viljanen 2003) compared the effects of behavioural interventions and no treatment on sick leave at short term. When we pooled the results of Dellve 2011 and Viljanen 2003, we found no differences (SMD 0.02, 95% CI -0.21 to 0.24; Analysis 5.5), nor did Sandsjö 2010 (RR 1.05, 95% CI 0.79 to 1.41; Analysis 5.6).
We conclude that moderate-quality evidence (downgraded by imprecision) shows that in the short term behavioural interventions lead to similar effects on sick leave as no treatment.
Nine of the remaining included studies (Abasolo 2005; Andersen 2008a; Bru 1994; Hagberg 2000; Kamwendo 1991; Marangoni 2010; Rempel 2007; Ripat 2006; Stralka 1998) did not provide data and therefore are not included in the comparisons above.
One other study (Meijer 2006) evaluated a multi-disciplinary treatment including physical exercises and relaxation treatment compared with usual care and found a statistically non-significant benefit in favour of the multi-disciplinary treatment (SMD -2.2, 95% CI -3.08 to 1.32) for pain at short term.
One study (Levoska 1993) compared the recovery-improving effects of exercise and massage and found no differences in effectiveness between exercise and massage (RR 0.78, 95% CI 0.55 to 1.11; Analysis 2.5). Another study (Leboeuf 1987) evaluated manual therapy compared with manual therapy plus massage and found the combination reducing symptom severity more than manual therapy alone (RD 0.4, 95% CI 0.11 to 0.69).
One study evaluated the use of a splint as add-on treatment to video education in participants with carpal tunnel syndrome (Werner 2005) and found no benefit of the additional splint for symptom severity score at short term (SMD -0,31, 95% CI -0.62 to 0). Another study evaluated low-frequency electrical stimulation versus placebo in participants with epicondylitis (Nourbakhsh 2008) and found significant short-term pain relief associated with the electrical stimulation (SMD -1.27, 95% CI -2,32 to -0.23).
One study (Bang 2000) compared exercise versus exercise and manual therapy in participants with an impingement syndrome (shoulder pain). Investigators found significant pain reduction and disability reduction (SMD 0.8, 95% CI 0.2 to 1.4 for pain; SMD 0.8, 95% CI 0.2 to 11.3 for disability) for exercise plus manual therapy at short term. Another study (Ylinen 2007) compared exercise versus manual therapy and found no difference (SMD 0, 95% CI -0.35 to 0.35) in pain at short-term follow-up.
One study compared amitriptyline, that is, pain medication, versus placebo in participants with non-specific neck and shoulder pain (Goldman 2010) and found no differences between the two groups in terms of pain at short-term follow-up (SMD 0.06, 95% CI -0.31 to 0.42).
Summary of main results
In total, we included 44 studies and 6,580 participants in this review. The studies had an overall high risk of bias. We judged only nine studies to have a low risk of bias.
Overall we found no clear benefit of exercise over no treatment or discussion controls or as additional treatment for pain, disability or sick leave. In participants with chronic non-specific complaints, regular exercises relieve pain more in the short-term when compared with specific exercises. We found no differences in disability or recovery.
The placebo keyboard seems to be more effective than experimental keyboards in reducing pain and disability and improving recovery. Ergonomic interventions reduced pain at long term, but not at short term. Also, ergonomic interventions seem to reduce pain but not disability in subacute participants and in participants with rotator cuff syndrome, when compared with no treatment. None of the ergonomic interventions provided greater benefit compared with another, or compared with placebo, on any of the outcome measures.
Overall, behavioural interventions did not show benefit when compared with no treatment, waiting list controls or other behavioural interventions, except for short-term pain when compared with waiting list controls.
Overall completeness and applicability of evidence
The aim of this review was to summarise existing evidence concerning the efficacy of frequently performed interventions in work-related neck, arm or shoulder musculoskeletal disorders (CANS). We applied a broad search strategy aimed at finding all trials that included people suffering from work-related CANS. No specific search strategy can be used to select participants with work-related complaints, mostly because defining which disorders are work-related appears to be rather difficult. Therefore, two independent review authors checked a large number of references.
Quality of the evidence
We considered only nine of the included studies to have low risk of bias. Most studies (n = 22) lacked information on the randomisation procedure and the analysis. Furthermore, blinding was difficult in these pragmatic studies.
Heterogeneity is another problem. We included several main groups of interventions, of which exercise was the largest. Each of these intervention groups consisted of a large variety of interventions and outcome measures. Although we were able to include 44 trials, it is disappointing that we could present so little evidence on the effects of interventions for CANS. In part, this is a result of the many different interventions available and the presentation of both short-term and long-term results, and it also reflects the overall high risk of bias. We found hardly any clinical heterogeneity in the study populations selected for inclusion in the original trials. Most studies included participants with chronic non-specific neck or shoulder complaints. CANS is mostly divided into specific and non-specific disorders, and the latter appear to constitute the larger group. This review contributes especially to the body of knowledge on non-specific work-related disorders.
Furthermore, 19 studies had small sample sizes (fewer than 25 participants in the smallest treatment arm). Although sample size does not contribute to the assessment of study risk of bias, it does show that most studies included in this review were underpowered to provide clear answers.
Potential biases in the review process
One of the possible biases of this review is selection bias. The most important difficulties include lack of a definition of work-relatedness, the wide variety of interventions used to treat people with possible CANS and the overall poor methodological quality. There is no clear definition of the work-relatedness of complaints. In the included trials, we noticed that defining the study population in this regard appeared to be difficult and subjective. Therefore, we might have missed studies that could have been included in this review.
The inconsistency in study results can also be due to our categorisation of studies into broad intervention categories. Even though we did our best to make the comparisons as homogeneous as possible, considerable variation is evident in intervention intensity and compliance. For example, Takala 1994 provided low-intensity exercises and Szcurko 2009 high-intensity training. However, a few studies (Ma 2011; Omer 2003) were clear outliers with exceptionally beneficial results that we could not explain by intervention intensity or compliance. The same argument holds for the category of ergonomic studies, which included a variety of interventions. Here too, we could find no proper explanation for the variable results. Heterogeneity could also have been the result of combining studies on all parts of the upper limb, neck and shoulder, but this did not explain the most pronounced differences in results.
Agreements and disagreements with other studies or reviews
The relevance of this systematic review in contributing to the body of knowledge concerning the efficacy of interventions in non-specific work-related CANS lies mainly in the fact that it points out a clear lack of evidence regarding the effectiveness of the interventions most often prescribed.
Although this version of the review includes 21 additional trials in comparison with the previous version (Verhagen 2006), the main conclusion of not finding clear evidence for the effectiveness of any treatment still holds. Some results of this updated review are slightly different compared with findings of the previous review. Our conclusion is in line with that of a large systematic review on the benefit of exercise for people with neck pain (Smidt 2005).
Implications for practice
This review concludes that low- to very low-quality evidence indicates that exercise does not provide a clear benefit over no treatment or discussion controls or as additional treatment for pain, disability or sick leave for people with work-related complaints of the arm, neck or shoulder. Specific exercises are less effective than regular ones. We also found low-quality evidence suggesting that ergonomic interventions in the workplace and behavioural interventions lead to similar results to those obtained with no or alternative interventions.
Implications for research
In this review, we evaluated a working population with a complaint. This complaint is not necessarily work-related. We need an agreed upon definition of what can be considered a work-related disorder. When consensus is reached, a clear participant population can be selected for future studies.
Future research should examine clear and well-defined interventions and especially should compare the intervention versus a no treatment control group.
Larger and adequately powered trials are needed that will focus on appropriate allocation concealment; blinding, if possible, of participant and therapist, or keeping them naive; and adequate data presentation and analysis.
We thank Helen Handoll, Co-ordinating Editor of the Bone, Joint and Muscle Trauma Review Group, and Jos Verbeek, Co-ordinating Editor of the Cochrane Occupational Safety and Health Review Group, for their valuable comments and advice. We also thank Lesley Gillespie for her help with the search strategies, and Joanne Elliott, Lindsey Elstub and Amy Kavanagh for their help and comments about the protocol. We thank Jani Ruotsalainen, Managing Editor of the Cochrane Occupational Safety and Health Review Group, for his extensive comments on and editing of the review text. Finally, we thank Dolores Matthews for copy editing the text.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- Contributions of authors
- Declarations of interest
- Sources of support
- Index terms
Appendix 1. Search strategies
The Cochrane Central Register of Controlled Trials (Wiley InterScience interface)
#1 MeSH descriptor Cumulative Trauma Disorders explode all trees
#2 MeSH descriptor Occupational Diseases, this term only
#3 MeSH descriptor Hand-Arm Vibration Syndrome, this term only
#4 MeSH descriptor Occupational Health, this term only
#5 ((occupational overuse or tension neck) NEXT syndrome):ti,ab
#6 (cumulative trauma*):ti,ab
#7 (work related):ti,ab
#8 (repetit* NEXT (strain or stress or industr* or motion or movement or trauma)):ti,ab
#9 (vibration NEXT (induced or related or syndrome*)):ti,ab
#10 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8 OR #9)
#11 MeSH descriptor Neck Pain, this term only
#12 MeSH descriptor Shoulder Pain, this term only
#13 MeSH descriptor Hand Injuries explode all trees
#14 MeSH descriptor Wrist Injuries, this term only
#15 MeSH descriptor Musculoskeletal Diseases, this term only
#16 (neck* or shoulder* or arm* or upper limb* or upper extremit* or elbow* or forearm* or wrist* or hand* or finger*):ti,ab
#17 (carpal tunnel syndrome*):ti,ab
#18 (#11 OR #12 OR #13 OR #14 OR #15 OR #16 OR #17)
#19 (#10 AND #18)
MEDLINE (Ovid interface)
1. exp Cumulative Trauma Disorders/
2. Occupational Diseases/ or Hand-Arm Vibration Syndrome/
3. Occupational Health/
4. ((occupational overuse or tension neck) adj syndrome).tw.
5. cumulative trauma$.tw.
6. work related.tw.
7. (repetit$ adj (strain or stress or industr$ or motion or movement or trauma)).tw.
8. (vibration adj (induced or related or syndrome$)).tw.
10. Neck Pain/ or Shoulder Pain/ or exp Hand Injuries/ or Wrist Injuries/
11. Musculoskeletal Diseases/
12. (neck$1 or shoulder$1 or arm$1 or upper limb$1 or upper extremit$ or elbow$1 or forearm$1 or wrist$1 or hand$1 or finger$1).tw.
13. Carpal Tunnel Syndrome/ or carpal tunnel syndrome$.tw.
16. Randomized Controlled Trial.pt.
17. Controlled Clinical Trial.pt.
20. Clinical Trials as Topic/
24. exp animals/ not humans/
25. 23 not 24
('Cumulative Trauma Disorder'/exp OR ('Occupational Disease':de OR 'Hand Arm Vibration Syndrome':de) OR 'Occupational Health':de OR (('occupational overuse' OR 'tension neck') NEAR/1 syndrome*):ti,ab,de OR (cumulative NEAR/1 trauma*):ti,ab,de OR 'work related':ti,ab,de OR (repetitive NEAR/1 (strain* OR stress* OR industr* OR motion* OR movement* OR trauma*)):ti,ab,de OR (vibration NEAR/1 (induced OR related OR syndrome*)):ti,ab,de) AND ('Neck Pain':de OR 'Shoulder Pain':de OR 'Hand Injury':de OR 'Wrist Injury':de OR 'Musculoskeletal Disease':de OR neck:ti,ab,de OR shoulder:ti,ab,de OR arm:ti,ab,de OR 'upper limb':ti,ab,de OR (upper NEAR/1 extremit*):ti,ab,de OR elbow*:ti,ab,de OR forearm:ti,ab,de OR wrist:ti,ab,de OR hand:ti,ab,de OR finger:ti,ab,de OR thumb:ti,ab,de OR necks:ti,ab,de OR shoulders:ti,ab,de OR arms:ti,ab,de OR 'upper limbs':ti,ab,de OR elbow*s:ti,ab,de OR forearms:ti,ab,de OR wrists:ti,ab,de OR hands:ti,ab,de OR fingers:ti,ab,de OR thumbs:ti,ab,de OR ('carpal tunnel' NEAR/1 syndrome*):ti,ab,de) AND ('randomized controlled trial'/de OR 'controlled clinical trial'/de OR random*:ti,ab OR placebo:ti,ab OR 'clinical trial'/de OR trial:ti) NOT ('animal'/exp NOT 'human'/exp)
Appendix 2. Criteria for a judgement of 'Yes' for the sources of risk of bias (see Table 1)
1. Was the method of randomisation adequate?
A random (unpredictable) assignment sequence. Examples of adequate methods are coin toss (for studies with two groups), rolling of a dice (for studies with two or more groups), drawing of balls of different colours, drawing of ballots with the study group labels from a dark bag, computer-generated random sequence, pre-ordered sealed envelopes, sequentially ordered vials, telephone call to a central office and pre-ordered list of treatment assignments.
Examples of inadequate methods include alternation, birth date, social insurance/security number, date on which they are invited to participate in the study and hospital registration number.
2. Was the treatment allocation concealed?
Assignment was generated by an independent person not responsible for determining the eligibility of patients. This person has no information about the persons included in the trial and has no influence on the assignment sequence or on the decision about eligibility of the patient.
Was knowledge of the allocated interventions adequately prevented during the study?
3. Was the participant blinded to the intervention?
This item should be scored 'Yes' if index and control groups were indistinguishable for the participants, or if the success of blinding was tested among the participants and it was successful.
4. Was the care provider blinded to the intervention?
This item should be scored 'Yes' if index and control groups were indistinguishable for the care providers, or if the success of blinding was tested among the care providers and it was successful.
5. Was the outcome assessor blinded to the intervention?
Adequacy of blinding should be assessed for the primary outcomes. This item should be scored 'Yes' if the success of blinding was tested among the outcome assessors and it was successful, or:
- For participant-reported outcomes for which the participant is the outcome assessor (e.g. pain, disability): The blinding procedure is adequate for outcome assessors if participant blinding is scored 'Yes'.
- For outcome criteria assessed during scheduled visit and that suppose a contact between participants and outcome assessors (e.g. clinical examination): The blinding procedure is adequate if participants are blinded, and if the treatment or adverse effects of the treatment cannot be noticed during clinical examination.
- For outcome criteria that do not suppose a contact with participants (e.g. radiography, magnetic resonance imaging): The blinding procedure is adequate if the treatment or adverse effects of the treatment cannot be noticed when the main outcome is assessed.
- For outcome criteria that are clinical or therapeutic events that will be determined by the interaction between participants and care providers (e.g. co-interventions, hospitalisation length, treatment failure), in which the care provider is the outcome assessor: The blinding procedure is adequate for outcome assessors if item 'E' is scored 'Yes'.
- For outcome criteria that are assessed from data extracted from the medical forms: The blinding procedure is adequate if the treatment or adverse effects of the treatment cannot be noticed in the extracted data.
Were incomplete outcome data adequately addressed?
6. Was the dropout rate described and acceptable?
The number of participants included in the study but who did not complete the observation period or were not included in the analysis must be described and reasons given. If the percentage of withdrawals and dropouts does not exceed 20% for short-term follow-up and 30% for long-term follow-up and does not lead to substantial bias, a 'Yes' is scored. (N.B. These percentages are arbitrary, not supported by literature.)
7. Were all randomly assigned participants analysed in the group to which they were allocated?
All randomly assigned participants are reported/analysed in the group to which they were allocated by randomisation for the most important moments of effect measurement (minus missing values), irrespective of non-compliance and co-interventions.
8. Are reports of the study free of suggestion of selective outcome reporting?
To receive a ‘Yes’, the review author determines whether all results from all prespecified outcomes have been adequately reported in the published report of the trial. This information is obtained by comparing the protocol and the report or, in the absence of the protocol, by assessing that the published report includes enough information to make this judgement.
Other sources of potential bias
9. Were the groups similar at baseline regarding the most important prognostic indicators?
To receive a 'Yes', groups have to be similar at baseline regarding demographic factors, duration and severity of complaints, percentage of participants with neurological symptoms and value of main outcome measure(s).
10. Were co-interventions avoided or similar?
This item should be scored 'Yes' if there were no co-interventions, or if they were similar between index and control groups.
11. Was the compliance acceptable in all groups?
The review author determines whether compliance with the interventions is acceptable, based on reported intensity, duration, number and frequency of sessions for both the index intervention and control intervention(s). For example, physiotherapy treatment is usually administered over several sessions; therefore, it is necessary to assess how many sessions each participant attended. For single-session interventions (e.g. surgery), this item is irrelevant.
12. Was the timing of the outcome assessment similar in all groups?
Timing of outcome assessment should be identical for all intervention groups and for all important outcome assessments.
Contributions of authors
APV, SMAB-Z, AB, HCWdV and BWK are responsible for drafting the protocol. The search was performed by APV, SMS, HCWdV and BWK, and selection of the studies and data extraction by APV, SMS and SMAB-Z. APV and AB are responsible for the analysis. All authors are responsible for the interpretation of results and for the final draft of the review.
Declarations of interest
Sources of support
- Erasmus Medical Centre, University, Netherlands.Salary and time to enable the review authors to perform the review
- No sources of support supplied
Medical Subject Headings (MeSH)
*Physical Therapy Modalities; Amitriptyline [therapeutic use]; Analgesics, Non-Narcotic [therapeutic use]; Arm; Behavior Therapy [methods]; Cumulative Trauma Disorders [*therapy]; Human Engineering [methods]; Massage; Neck; Occupational Diseases [*therapy]; Randomized Controlled Trials as Topic; Shoulder; Sick Leave [statistics & numerical data]
MeSH check words
* Indicates the major publication for the study