Efficacy of different types of aerobic exercise in fibromyalgia syndrome: a systematic review and meta-analysis of randomised controlled trials

Methods of analysis and inclusion criteria were specified in advance. We used the review protocol of our systematic review on multicomponent therapy in FMS [16].

The electronic bibliographic databases screened included the Cochrane Central Register of Controlled Trials (CENTRAL), EMBASE, MEDLINE, PsychInfo and SPORTDISCUS (through 31 March 2009). The search strategy for MEDLINE is detailed in Additional file 1. The search strategy was adapted for each database as necessary. No language restrictions were made. Only fully published papers were reviewed. In addition, reference sections of original studies, systematic reviews [8‐10] and evidence-based guidelines on the management of FMS [4‐6] were screened manually.

The search was conducted by two authors (PK, JL). Two authors screened the titles and the abstracts of potentially eligible studies identified by the search strategy detailed above independently (PK, JL). The full-text articles were then examined independently by two authors to determine whether they met the selection criteria (MSc, JL). Discrepancies were rechecked and consensus was achieved by discussion. If needed, two other authors reviewed the data to reach a consensus (AB, WH).

Two authors independently extracted the data using standard extraction forms [16] (BM, MSc). Discrepancies were rechecked and consensus was achieved by discussion. If needed, a third author reviewed the data to reach a consensus (WH).

Based on our experiences of former systematic reviews in which none of the contacted authors provided these details on request, we did not ask for clarifications of study design in case of unclear randomisation, blinding or concealment of treatment allocation. We searched for further details of the study design in a Cochrane review [12].

When means or standard deviations (SDs) were missing, attempts were made to obtain these data through contacting 12 trial authors. Additional data were provided by four authors (see Tables 1 and 2). Where SDs were not available from the trial authors, they were calculated from t values, confidence intervals or standard errors when reported in articles [15]. If only the median was given, the median was used instead of the mean and a SD was substituted that was calculated as the mean of the SDs available for studies that used the same outcome scale.

The data for the study setting, participants, exclusion criteria, interventions, co-therapies, attendance rates, side effects reported and outcomes sought are presented in Tables 2 and 3.

When researchers reported more than one measure for an outcome, we used a predefined order of preference for analysis (details available on request).

If studies had two or more potential control groups, we used the following order to select for control group: treatment as usual, attention placebo, and active control to select the control group.

To ascertain the internal and external validity of the eligible RCTs, two pairs of reviewers (BM, WH; and MSc, Mst) working independently and with adequate reliability determined the adequacy of randomisation, concealment of allocation, blinding of outcome assessors and adequacy of data analysis (was intention-to-treat-analysis performed?) (internal validity). Furthermore we chose the item 'Were patients with mental disorders frequently associated with FMS (depressive and anxiety disorders) included in the studies?' as the marker of external validity.

Meta-analyses were conducted using RevMan Analyses software (RevMan 5.0.17) from the Cochrane collaboration [18]. Standardised mean differences (SMDs) were calculated by means and SDs or change scores for each intervention. The SMD used in Cochrane reviews is the effect size known as Hedge's (adjusted) g [15]. Examination of the combined results was performed by a random effects model (inverse variance method), because this model is more conservative than the fixed effects model and incorporates both within-study and between-study variance [19]. We used Cohen's categories to evaluate the magnitude of the effect size, calculated by the SMD: g > 0.2 to 0.5, small effect size; g > 0.5 to 0.8, medium effect size; g > 0.8, large effect size [20].

Heterogeneity was tested using the I² statistic, with I² > 50% indicating strong heterogeneity. τ² was used to determine how much heterogeneity was explained by subgroup differences [15].

Potential publication bias - that is, the association of publication probability with the statistical significance of study results - was investigated using visual assessment of the funnel plot (plots of effect estimates against its standard error) calculated by RevMan Analyses software. Publication bias may lead to asymmetrical funnel plots [15]. Moreover, we checked a potential small sample size bias by a sensitivity analysis of studies with very small (<25), small (25 to 50) and medium (>50) sample sizes.

The literature search produced 464 citations, of which 292 were double hits (study found in at least two data sources). By screening, 110 records were excluded: 23 evaluated AE, but not in FMS; 19 did not evaluate AE in FMS; 52 were review articles; and 18 were case reports or commentaries. Sixty of the full-text articles assessed for eligibility, and 25 full-text articles were excluded for the following reasons: two for publication of different outcomes of one trial in two publications [21, 22]; six for lacking a control group [23‐28]; three for lacking randomisation [29‐31]; two because one could not conclude from the study protocol that the exercises performed met the predefined criteria of AE [32, 33]; one because two different types of water-based exercise with similar intensity were compared [34]; one because the study did not assess a primary outcome measure [35]; and 10 because AE was combined with education or psychotherapy or pharmacotherapy [36‐45]. Three RCTs comparing different intensities of AE [46‐48], four RCTs comparing land-based with water-based exercise [49‐52] and 28 RCTs with 29 study arms comparing AE with controls [53‐80] were included in the qualitative and quantitative analyses (see Figure 1).

Only two studies fulfilled all predefined criteria of internal and external validity (see Table 1).

The means, SDs, sample sizes and effect estimates of each study can be seen in the forest plots (see Additional files 4, 5, 6, 7, 8, 9, 10, 11, 12 and 13).

There was only substantial heterogeneity in the comparisons of depressed mood and HRQOL at post treatment and for depressed mood at latest follow-up (see Table 2). On visual inspection, the funnel plots of the outcomes post treatment were symmetrical and were thus not indicative for a publication bias (see Additional file 14). Studies with small sample sizes had no significant effect on pain at post treatment (see Table 5).

AE reduces pain, fatigue and depressed mood, and improves HRQOL and physical fitness, at post treatment. Positive effects of AE on depressed mood, HRQOL and physical fitness can be detected at latest follow-up. AE has no positive effect on sleep at post treatment, and on pain, fatigue and sleep at follow-up. Continuing exercise is necessary to maintain positive effects on pain.

The following statements are valid for pain reduction at post treatment. There is no evidence of a superiority of water-based over land-based exercise. AE with a slight to moderate intensity is effective. Low-intensity AE (<50% maxHR) is not effective. A frequency of AE of 2 to 3 times/week for at least 4 to 6 weeks is necessary for a reduction of symptoms. Combining AE with stretching or strengthening is no more effective than AE alone.

The evidence is applicable to the majority of patients in clinical practice except patients with internal and orthopaedic diseases that may prevent AE and male patients.

Although every effort was made to obtain missing data (outcomes, study design) from the trial authors, it was not possible in every case to obtain these data; the included studies are therefore not represented fully in the meta-analyses. Only medians were available for three studies, but excluding these studies from analysis did not change the results.

The exercise protocol was insufficiently reported by some trials. The positive effects of the training can therefore possibly be attributed to other forms of exercise such as strength, stretching or relaxation, or in the case of pool-based exercise to the effects of warm water. Subgroup analyses did not, however, show a superiority of mixed exercise versus aerobic exercise nor a superiority of pool-based exercise versus land-based exercise.

The prescribed training intensity was either not assessed by heart rate telemetry or was not reported. No definitive conclusions on an effective intensity of AE are therefore possible.

The attendance rates during the study were inconsistently reported. If continuation of exercise until follow-up was recommended was inconsistently reported too. A subgroup analysis of studies with and without recommended exercise at follow-up was thus not possible.

Side effects were inconsistently reported. No definitive statement on the safety of AE in FMS is therefore possible.

The methodological quality of the studies varied. The positive effect on pain, however, was robust against potential methodological biases.

Given that formal blinding of participants and clinicians to the treatment arm is not possible in trials of exercise, we could have underestimated the extent to which clinicians' and participants' knowledge of group assignation influenced the true effect.

Males and adolescents were rarely included in the study populations. As no gender comparisons were reported, the evidence for the efficacy of AE in men and adolescents with FMS is limited.

The amount and intensity of initial AE should be adapted to the individual level of physical fitness. Patients should start at levels just below their capacity and gradually increase the duration and intensity until they are exercising with low to moderate intensity for 20 to 30 minutes 2 to 3 times/week [12]. It does not seem necessary to assess the heart rate during AE to find the optimum intensity. Patients should exercise with an intensity at which they are able to speak fluently with another person [17]. The choice of the type of AE should be left to the patient's preferences and comorbidities and to the local offers of AE [11]. A training programme should last a minimum of 4 weeks. Patients should be educated that they may have some tolerable short-term increases in pain and fatigue but, if they exercise at an appropriate intensity, these symptoms should return to baseline levels within the first few weeks of exercise [12, 17]. Patients should be motivated to continue exercise if they perceive a reduction of symptoms after the programme.

Because AE does not reduce sleeping disturbances, a combination of AE with medication effective for improving sleep - for example, tricyclic or dual antidepressants or pregabalin [81, 82] - should be considered.

Four main questions need to be answered by future studies. By which methods (for example, education, booster sessions) can patients be motivated to continue exercise? Is aerobic and mixed exercise cost-effective [83]? Is the combination of AE with pharmacological therapy superior to AE or medication alone? Which sociodemographic and clinical variables predict a positive and negative treatment outcome?

Future studies on these topics should focus on larger sample sizes (multicentre studies including a sufficient number of men and adolescents and patients with mental and somatic comorbidities). Study quality could be improved by detailed reporting of demographic and clinical data of the study groups at baseline, exercise protocol and adherence to interventions (attendance rates, adherence to prescribed intensity assessed by heart rate telemetry), creation of a standardised protocol to report adverse events and use of standard outcome measures.