Non‐pharmacological interventions for fatigue in rheumatoid arthritis
Abstract
Background
Fatigue is a common and potentially distressing symptom for people with rheumatoid arthritis with no accepted evidence based management guidelines. Non‐pharmacological interventions, such as physical activity and psychosocial interventions, have been shown to help people with a range of other long‐term conditions to manage subjective fatigue.
Objectives
To evaluate the benefit and harm of non‐pharmacological interventions for the management of fatigue in people with rheumatoid arthritis. This included any intervention that was not classified as pharmacological in accordance with European Union (EU) Directive 2001/83/EEC.
Search methods
The following electronic databases were searched up to October 2012, Cochrane Central Register of Controlled Trials (CENTRAL); MEDLINE; EMBASE; AMED; CINAHL; PsycINFO; Social Science Citation Index; Web of Science; Dissertation Abstracts International; Current Controlled Trials Register; The National Research Register Archive; The UKCRN Portfolio Database. In addition, reference lists of articles identified for inclusion were checked for additional studies and key authors were contacted.
Selection criteria
Randomised controlled trials were included if they evaluated a non‐pharmacological intervention in people with rheumatoid arthritis with self‐reported fatigue as an outcome measure.
Data collection and analysis
Two review authors selected relevant trials, assessed risk of bias and extracted data. Where appropriate, data were pooled using meta‐analysis with a random‐effects model.
Main results
Twenty‐four studies met the inclusion criteria, with a total of 2882 participants with rheumatoid arthritis. Included studies investigated physical activity interventions (n = 6 studies; 388 participants), psychosocial interventions (n = 13 studies; 1579 participants), herbal medicine (n = 1 study; 58 participants), omega‐3 fatty acid supplementation (n = 1 study; 81 participants), Mediterranean diet (n = 1 study; 51 participants), reflexology (n = 1 study; 11 participants) and the provision of Health Tracker information (n = 1 study; 714 participants). Physical activity was statistically significantly more effective than the control at the end of the intervention period (standardized mean difference (SMD) ‐0.36, 95% confidence interval (CI) ‐0.62 to ‐0.10; back translated to mean difference of 14.4 points lower, 95% CI ‐4.0 to ‐24.8 on a 100 point scale where a lower score means less fatigue; number needed to treat for an additional beneficial outcome (NNTB) 7, 95% CI 4 to 26) demonstrating a small beneficial effect upon fatigue. Psychosocial intervention was statistically significantly more effective than the control at the end of the intervention period (SMD ‐0.24, 95% CI ‐0.40 to ‐0.07; back translated to mean difference of 9.6 points lower, 95% CI ‐2.8 to ‐16.0 on a 100 point scale, lower score means less fatigue; NNTB 10, 95% CI 6 to 33) demonstrating a small beneficial effect upon fatigue. For the remaining interventions meta‐analysis was not possible and there was either no statistically significant difference between trial arms or findings were not reported. Only three studies reported any adverse events and none of these were serious, however, it is possible that the low incidence was in part due to poor reporting. The quality of the evidence ranged from moderate quality for physical activity interventions and Mediterranean diet to low quality for psychosocial interventions and all other interventions.
Authors' conclusions
This review provides some evidence that physical activity and psychosocial interventions provide benefit in relation to self‐reported fatigue in adults with rheumatoid arthritis. There is currently insufficient evidence of the effectiveness of other non‐pharmacological interventions.
PICOs
Plain language summary
Non‐pharmacological interventions for the management of patient‐reported fatigue in rheumatoid arthritis
This summary of a Cochrane review presents what we know from research that has investigated the effects of non‐pharmacological treatments for fatigue in people with rheumatoid arthritis.
After searching for all relevant studies, 24 were identified for inclusion in the review with a total of 2882 people. The findings are summarised as follows.
‐ Physical activity has a small benefit for managing fatigue in people with rheumatoid arthritis.
‐ Psychosocial therapy has a small benefit for managing fatigue in people with rheumatoid arthritis.
‐ No other interventions showed a difference in managing fatigue in people with rheumatoid arthritis. This may have happened by chance.
The information available regarding side effects and complications of the interventions was not very informative although it is unlikely that any side effects would cause a serious problem.
What is rheumatoid arthritis and what are non‐pharmacological interventions?
When you have rheumatoid arthritis, your immune system, which normally fights infection, attacks the lining of your joints. This makes your joints swollen, stiff and painful. The small joints of your hands and feet are usually affected first. There is no cure for rheumatoid arthritis at present, so the treatments aim to relieve pain and stiffness and improve your ability to move. Fatigue is also a problem for people with rheumatoid arthritis.
Non‐pharmacological interventions include any treatment that is not a registered drug, such as physical activity and psychosocial interventions (talking therapies). A talking therapy could include meeting with a counsellor, alone or in a group. It might involve writing about your thoughts and feelings in a journal and talking about it, problem‐solving, setting goals and getting feedback about self‐management. It might also include sessions on pain management and relaxation; and coping with depression. There are other non‐pharmacological treatments that have been tested for their effect upon fatigue in people with rheumatoid arthritis. These include different dietary supplements and studies on the effects of giving people access to information about their own disease status. These treatments if supported by the overall body of evidence would allow the patient to have some personal control of their fatigue.
What happens to people with rheumatoid arthritis who use non‐pharmacological interventions?
‐ At the end of the intervention, people receiving a control had a mean score of 63 on a scale of 0 to 100 with a lower score meaning less fatigue.
‐ People who used physical activity rated their fatigue as 54 on a scale of 0 to 100 at the end of the intervention, that is 9 points lower than the people who received the control.
‐ People who participated in a psychosocial intervention rated their fatigue as 57 on a scale of 0 to 100 at the end of the intervention, that is 6 points lower than the people who received the control.
Authors' conclusions
Summary of findings
| Non‐pharmacological interventions for rheumatoid arthritis | ||||||
| Patient or population: patients with rheumatoid arthritis | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | No of Participants | Quality of the evidence | Comments (95% CI) | |
| Assumed risk | Corresponding risk | |||||
| Control | Non‐Pharmacological Interventions | |||||
| fatigue (physical activity interventions) | The mean fatigue in the control groups was | The mean fatigue (physical activity interventions) in the intervention groups was | 371 | ⊕⊕⊕⊝ | SMD ‐0.36 (‐0.62 to ‐0.10) Relative percent change ‐13.7% (‐23.6 to ‐3.8) NNTB 7 (4 to 26) | |
| fatigue (psychosocial interventions) | The mean fatigue in the control groups was | The mean fatigue (psychosocial interventions) in the intervention groups was | 1,556 | ⊕⊕⊝⊝ | SMD ‐0.24 (‐0.40 to ‐0.07) Relative percent change ‐9.1% (‐15.2 to ‐2.7) NNTB 10 (6 to 33) | |
| fatigue (Andrographis paniculata) | The mean fatigue in the control groups was | The mean fatigue (Andrographis Paniculata) in the intervention groups was | 58 | ⊕⊕⊝⊝ | SMD ‐0.25 (‐0.77 to 0.27) Relative percent change ‐9.5% (‐29.3 to 10.3) NNTB not applicable | |
| fatigue (data tracker) | The mean fatigue in the control groups was | The mean fatigue (data tracker) in the intervention groups was | 714 | ⊕⊕⊝⊝ | SMD 0.06 (‐0.10 to 0.21) Relative percent change 2.3% (‐3.8 to 8.0) NNTB not applicable | |
| fatigue (Omega‐3 Fatty acids) | The mean fatigue in the control groups was | The mean fatigue (Omega‐3 Fatty acids) in the intervention groups was | 81 | ⊕⊕⊝⊝ | SMD 0.93 (0.47 to 1.39) Relative percent change 35.4% (17.9 to 53.0) NNTB not applicable | |
| fatigue (Mediterranean diet) | The mean fatigue in the control groups was | The mean fatigue (Mediterranean diet) in the intervention groups was | 51 | ⊕⊕⊕⊝ | SMD 0.37 (‐0.18 to 0.93) Relative percent change 14.1% (‐6.9 to 35.4) NNTB not applicable | |
| fatigue (reflexology) | The mean fatigue in the control group was 6.3 VAS (score: 0‐10) | The mean fatigue (Reflexolgy) in the intervention groups was | 11 (1 study) | ⊕⊕⊝⊝ | SMD ‐1.24 (‐2.59 to 0.11) Relative percent change ‐47.2% (‐98.7 to 4.2) NNTB not applicable | |
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1 A lower score means less fatigue 2 Based on a conversion from Hewlett S et al (Mean: 6.3, SD: 2.4). | ||||||
Background
Description of the condition
Rheumatoid arthritis (RA) is an auto‐immune, systemic, inflammatory condition causing pain and synovitis primarily in the joints of the hands and feet, but often involving additional joints (Conaghan 1999). Repeated flares of such disease activity cause symptoms of pain, fatigue, stiffness and long‐term loss of function. People with a range of long‐term conditions report clinically significant fatigue (for example multiple sclerosis, diabetes, stroke) and it has been identified by RA patients as a key problem, which they consider harder to manage than pain (Hewlett 2005). Quantitative studies consistently show that fatigue occurs in up to 70% of RA patients in the UK (almost 0.4 million people), and is as common and severe as pain (Department of Health 2006; Wolfe 1996). Fatigue has been identified by people with RA as a major concern (Hewlett 2005) and international consensus has been reached that it should be measured in all clinical trials (Kirwan 2007). Specifically, in 2008, participants including patients at OMERACT (Outcome Measures in Rheumatology) endorsed fatigue as an addition to the 'core set' of outcome measures for all future studies, highlighting the importance of this symptom (Kirwan 2007).
RA fatigue is likely to be explained by multiple and complex pathways that vary between and within patients over time (Hewlett 2011a). There is currently mixed evidence for the explanatory role of inflammatory activity and it is likely that additional causal pathways include behavioural activities (for example boom and bust behaviours where the individual does too much when they have some energy, resulting in feeling more fatigued, and then has to rest for longer), deconditioning from disability, mood (for example anxiety, depression, helplessness), illness beliefs (for example unrealistic outlook), stress and pain (Hewlett 2008; Pollard 2006; Treharne 2009). It is possible that the mixed evidence also arises from the lack of RA‐specific fatigue measures and is associated with the lack of an agreed fatigue definition at the time these studies were conducted (Hewlett 2011b).
Description of the intervention
Many non‐pharmacological approaches to the management of RA fatigue are used. These centre largely around, but are not restricted to, self‐management techniques based upon physical activity and psychosocial interventions. Non‐pharmacological interventions may be initiated or supported by education programmes by the multi‐disciplinary team using processes such as group education (Hewlett 2008). In terms of physical activity, interventions may include strategies to increase a person's overall daily activity level or the implementation of a specific exercise regime such as walking or cycling for a specific duration at a target intensity. Psychosocial interventions may include a range of talking therapies that are based upon a specific behaviour change theory. Previous Cochrane reviews have been carried out to investigate the effects of non‐pharmacological interventions in RA (Brosseau 2005; Cameron 2011; Casimiro 2002; Casimiro 2005; Egan 2001; Hagen 2009; Han 2004; Hurkmans 2009; Pelland 2002; Silva 2010; Tuntland 2009; Verhagen 2004; Welch 2002) but none have specifically investigated the effects of these interventions on fatigue.
How the intervention might work
Non‐pharmacological interventions may address several causal pathways at the same time. For example, education programmes may work by not only helping people to change behaviours that perpetuate RA fatigue or inhibit its self‐management, through pacing and lifestyle management, but also by addressing mood and coping strategies. Exercise interventions may address physiological deconditioning (either muscular or respiratory) that are associated with disability or inactivity in RA. Interventions that address thoughts and feelings around fatigue may encourage helpful coping strategies, such as emotional expression, reprioritisation and work and life balance, and help patients reduce perceived stress and helplessness. In addition, the mode of delivery of such interventions that is effective in bringing about behaviour change needs to be identified. For example, it has been shown in other Cochrane reviews of group education in musculoskeletal disease that a cognitive‐behavioural therapy approach is more likely to prompt the adoption of new behaviours than simple information giving (Riemsma 2003).
Why it is important to do this review
No systematic review of non‐pharmacological interventions to help people manage their RA fatigue has been conducted, therefore the question of whether or not they work has not been answered. Interventions such as group education as reported in the literature are time‐consuming and costly for patients and professionals, and need to be delivered in a way that results in behaviour change, therefore the evidence needs evaluating to enhance practice.
Objectives
To evaluate the benefit and harm of non‐pharmacological interventions for the management of fatigue in people with rheumatoid arthritis. This included any intervention that was not classified as pharmacological in accordance with European Union (EU) Directive 2001/83/EEC.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials
Types of participants
Adults (usually over 18 years of age) with a diagnosis of RA either confirmed by a rheumatologist or using American College of Rheumatology (ACR) criteria (Arnett 1988).
Types of interventions
All non‐pharmacological interventions, which encompassed all interventions other than those that were classified as pharmacological. Pharmacological interventions were classified as medicinal products in accordance with the EU Directive 2001/83/EEC (EU 2001) which states: "any substance or combination of substances which may be used in or administered to human beings either with a view to restoring, correcting or modifying physiological functions by exerting a pharmacological, immunological or metabolic action, or to making a medical diagnosis".
Because of the large number of possible non‐pharmacological interventions, each of which may have many synonyms, there was a risk of missing some interventions if only specific search terms were used. We therefore initially searched for any randomised controlled trial reporting RA fatigue and identified the non‐pharmacological interventions from those results.
The comparison arm could have been placebo, an alternative intervention (pharmacological or non‐pharmacological) or usual care, including no specific intervention for fatigue.
Types of outcome measures
Primary outcomes
The primary outcomes for this systematic review were self‐reported fatigue scores using validated measures, and adverse events. Adverse events were recorded as reported in the studies on the basis of the Cochrane definition of "harms associated with healthcare interventions". Distinctions were made between an adverse event (unfavourable outcome occurring during, but not necessarily caused by, the intervention), an adverse effect (reasonable possibility of causal relation) and a side effect (any unintended effect) (Cochrane Handbook for Systematic Reviews of Interventions sections 14.1.2 and 14.3.1) (Higgins 2011).
Secondary outcomes
Secondary outcomes were pain, anxiety, depression, disability and tender or swollen joints.
Search methods for identification of studies
The search strategies were developed for MEDLINE in line with recommendations from the Cochrane Musculoskeletal Review Group and are shown in Appendix 1. The search strategies were applied to all databases (adapted appropriately to suit the database style): EMBASE (Appendix 2); CENTRAL (Appendix 3); CINAHL (Appendix 4); PsycINFO (Appendix 5); AMED (Appendix 6); Web of Science (Appendix 7); and Dissertation Abstracts International (Appendix 8).
Electronic searches
The following electronic databases were searched:
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Cochrane Central Register of Controlled Trials (CENTRAL) (up to October 2012);
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MEDLINE (1966 to October 2012);
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EMBASE (1983 to October 2012);
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AMED (1985 to October 2012);
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CINAHL (1982 to October 2012);
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PsycINFO (1974 to October 2012);
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Social Science Citation Index (1990 to October 2012);
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Web of Science (1990 to October 2012);
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Dissertation Abstracts International (1871 to October 2012);
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Current Controlled Trials Register (USA) (up to October 2012);
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The National Research Register (NRR) Archive (UK) (up to October 2012);
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The UKCRN Portfolio Database (UK) (up to October 2012).
Searching other resources
In addition, reference lists of studies identified for inclusion in the review as well as previous review papers were handsearched to find additional studies, as was the Arthritis Research Campaign (arc) Topical Review on Fatigue in Musculoskeletal Disease (Hewlett 2008). Relevant authors in the field were contacted to ask about unpublished research that was not detected by the search strategies.
Data collection and analysis
Inclusion criteria
Randomised controlled trials of adults with confirmed RA (Arnett 1988) where fatigue was included as a primary or secondary outcome measure (and not just an adverse effect), reported separately for RA patients.
Exclusion criteria
Studies that only investigated pharmacological interventions.
Selection of studies
Titles and abstracts were assessed for all records identified through the search strategies. Two review authors examined each citation and full papers were retrieved for all those appearing to meet the inclusion criteria. Full reports were also acquired where there was any uncertainty surrounding their inclusion or where abstracts were not available and it was not possible to exclude the trial based on title alone. Where there were disagreements regarding eligibility the full text was retrieved. All full text articles were screened for the inclusion and exclusion criteria by two independent review authors and any disagreements as to eligibility were resolved by discussion and the involvement of an arbiter where necessary.
Data extraction and management
For each publication, two review authors (papers allocated according to expertise) independently retrieved the following details, tabulated on a standardized form: intervention (including characteristics and duration); details of the participants' health status; assignment to study arm (including process used, concealment and comparability of arms); outcome measures; timing of measurements; adherence to intervention and control, sample size and statistical analysis methods (including intention to treat).
Assessment of risk of bias in included studies
For each paper, the two review authors independently assessed methodological quality using individual components of quality from tools such as that provided by the Cochrane Collaboration. Individual components rather than summary scores have been recommended (Khan 2001) in non‐pharmacological trials where blinding of participants in a complex interaction has proved challenging, meaning that all such trials would score low for blinding. For such studies it was particularly important to assess whether obtaining outcome data was blinded.
The risk of bias of the included studies was also assessed by two independent review authors. As recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), the following methodological domains were assessed:
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sequence generation;
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allocation concealment;
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blinding of participants, personnel and outcome assessors;
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incomplete outcome data;
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selective outcome reporting; and
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other potential threats to validity (e.g. appropriate use of co‐interventions).
Each of these criteria were explicitly judged and classified as: low risk of bias; high risk of bias or unclear (either insufficient information or uncertainty over the potential for bias).
Assessment of the power of the study to detect changes in RA fatigue was made by examining the power calculations reported in the studies. Assessment of the validity of the fatigue measure used was made using the methods of Hewlett 2007.
Measures of treatment effect
We expected a range of fatigue outcome measures to have been used in the identified studies therefore we planned a priori to use standardised mean differences. The central estimate (mean) and standard deviation were recorded. Where the standard deviations were not explicitly stated, they were calculated from the standard error, the different means and their respective confidence intervals or P values. Where adverse events were given as dichotomous data, they were reported as the proportion of patients experiencing the event in each arm and comparisons made.
Unit of analysis issues
We expected some non‐pharmacological interventions to be delivered at the individual level, where the unit of analysis would be individual. Where interventions were delivered in groups, the group was the unit of analysis. However, group level interventions are often analysed and reported at an individual rather than group level, or without adjusting for group effect. Where these group data were not reported we contacted the authors for further information.
Dealing with missing data
Where change scores were not available these were sought from the authors. Where they were not available and the mean change could be calculated, standard deviations were imputed from baseline data using methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (section 16.1.3.2) (Higgins 2011).
We intended a priori to carry out an intention‐to‐treat analysis in studies where patients allocated to the intervention arm were included regardless of whether or not they completed the follow‐up. In these studies the assumption should have been made that patients who dropped out of the study had no changes in their outcomes, giving a conservative assessment of response to treatment. We requested further details from authors in cases where published data were incomplete.
Assessment of heterogeneity
Where appropriate, heterogeneity of the data was formally assessed using the I2 statistic (Higgins 2003). A value greater than 50% may represent substantial heterogeneity. Where substantial heterogeneity was detected, and there were sufficient studies available, subgroup analyses was proposed in an attempt to explain the heterogeneity.
Assessment of reporting biases
A funnel plot was used to assess the possibility of publication bias.
Data synthesis
Included studies were graded using the GRADE approach (Schünemann 2008), which employs the following rating system: randomised trials (high), downgraded randomised trials (moderate), double‐downgraded randomised trials (low) and triple‐downgraded randomised trials (very low). The quality ratings may be decreased by:
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limitations in the design and implementation of available studies suggesting high likelihood of bias;
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indirectness of evidence (indirect population, intervention, control, outcomes);
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unexplained heterogeneity or inconsistency of results (including problems with subgroup analyses);
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imprecision of results (wide confidence intervals); or
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high probability of publication bias.
We expected a mixture of changes from baseline and absolute study arm differences across a variety of measures of RA fatigue. We also expected some variation in methods of analysis, including the absolute difference compared between study arms, and baseline‐adjusted differences between arms. We followed the Cochrane Handbook for Systematic Reviews of Interventions guidelines (Higgins 2011) in section 9.4.5.2 in deciding which group of studies could be included in any meta‐analysis. We imputed standard deviations (SD) where necessary according to section 16.1.3.
In studies with multiple intervention arms the number of participants included in the control arm was divided by the number of intervention arms to avoid double counting. Where more than one fatigue outcome existed in a single study, visual analogue scale (VAS) data, if present, were selected for inclusion in the meta‐analysis. Where VAS data were not available data for the SF‐36 vitality scale were utilised. For any remaining studies with multiple fatigue outcome measures that did not include the VAS or SF36, the measure selected for use in the review was based upon the findings of a previous critical review of fatigue scales in RA (Hewlett 2007).
Where there was no heterogeneity a fixed‐effect model was used, and where there was heterogeneity a random‐effects model was proposed. When the outcome used or the number, quality or heterogeneity of existing trials contraindicated meta‐analysis, each study was reported and discussed individually using effect sizes for fatigue difference (differences divided by the SD) using Cohen’s statistic (0.2 to 0.5 = small effect, 0.5 to 0.8 = moderate, > 0.8 = large effect) (Cohen 1998).
Subgroup analysis and investigation of heterogeneity
Where sufficient studies were available and the data were heterogenous, meta‐analyses were carried out for studies using similar intervention approaches, for example exercise, self‐management education programmes, or cognitive‐behavioural therapy. A priori, the categories of physical activity and psychosocial interventions were expected to emerge from the available data. A conversion proposed by Chinn (Chinn 2000) was used to convert standardised mean differences (SMDs) into odds ratios (OR) with the control event rate estimated from Hewlett 2011c.
Sensitivity analysis
The following sensitivity analyses were planned a priori in order to explore differences in effect size and to assess whether the conclusions were robust to the decision‐making process:
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the effect of risk of bias in included studies, defined as adequate allocation concealment and blinding of outcome assessors; and
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the effect of imputing missing data or transforming variables.
Results
Description of studies
See: Characteristics of included studies; Characteristics of excluded studies
Results of the search
See: Figure 1
Study flow diagram.
Through a comprehensive literature search, including screening of titles and abstracts (where available), attempts were made to retrieve 60 full text references for further evaluation. From these, 37 publications were excluded and 23 identified as appropriate for inclusion in the current review. Screening of reference lists led to the retrieval of eight further full text studies. One of the eight was identified as appropriate for inclusion resulting in 24 studies in total. The 24 publications reported separate trials with one study (Giraudet‐Le‐Quintrec 2007) providing additional data in a separate report.
Included studies
The final selection, based on consensus, resulted in 24 trials being identified for inclusion in the review. The studies were published between 1985 and 2012. Three of the included studies (Danoff‐Burg 2006 ‐ I; Neuberger 2007 ‐ I; Riemsma 2003 ‐ I) incorporated three separate study arms and were therefore entered twice for the purpose of statistical analysis.
Participants
Overall, data were available for 2882 participants with RA. The number of participants completing the studies ranged from 11 (Otter 2010) to 714 (Huffstutter 2007).
The mean age of participants fell mainly within the fifth decade with five studies reporting a mean age in the mid to late 40s and two reporting the mean age to be in the 60s. One study specifically recruited housebound patients over the age of 50 years and subsequently reported a mean age of 77.7 years (Laforest 2008), whereas another study only recruited patients aged 18 to 35 years and reported a mean age of 28.3 years (Evans 2012). Two studies did not report the gender of participants (Das Gupta 2009; Otter 2010). Twenty of the remaining 23 studies recruited both males and females with 19 of these reporting a higher percentage of females and one not providing these data (Burgos 2009). However, three of the studies provided gender data for the entire population recruited with no specific gender data reported for participants with RA (Danoff‐Burg 2006 ‐ I; Lorig 2005; Zangi 2012). Two studies recruited females only (Evans 2012; Harkcom 1985).
Seventeen studies included participants with RA diagnosed according to the 1987 ACR criteria, four studies relied upon verification of RA by a clinician (Hammond 2008; Laforest 2008; Lorig 2005; Otter 2010), one study included participants based upon the American Rheumatism Association (ARA) 1958 guidelines (Harkcom 1985). The remaining two studies either did not clarify the method of diagnosing people with RA (Danoff‐Burg 2006 ‐ I) or did not employ a consistent approach to diagnosis (Lorig 2008).
Nine studies reported that participants' mean duration of disease was greater than 12 years (Hammond 2008; Harkcom 1985; Hewlett 2011; Huffstutter 2007; Lumley 2011‐I; Otter 2010; Skoldstam 2003; Wang 2008; Zangi 2012). Three studies reported the mean duration of disease as less than three years (Bilberg 2005; Danoff‐Burg 2006 ‐ I; Hakkinen 2003) and a further four studies did not report disease duration for the participants (Das Gupta 2009; Laforest 2008; Lorig 2005; Lorig 2008).
Interventions
See Table 1
| Study ID | Intervention category | Specific intervention |
| Physical activity | pool‐based therapy | |
| Physical activity | Yoga | |
| Physical activity | strength training | |
| Physical activity | stationary cycling | |
| Physical activity | aerobic exercise | |
| Physical activity | Tai Chi | |
| Psychosocial | benefit finding and expressive writing | |
| Psychosocial | cognitive skills training & written emotional disclosure | |
| Psychosocial | cognitive behavioural therapy | |
| Psychosocial | cognitive behavioural therapy | |
| Psychosocial | mindfulness based group intervention | |
| Psychosocial | lifestyle management | |
| Psychosocial | education incorporating energy conservation | |
| Psychosocial | education incorporating self management | |
| Psychosocial | education incorporating self management | |
| Psychosocial | education incorporating self management | |
| Psychosocial | group education | |
| Psychosocial | group education | |
| Psychosocial | group education | |
| Other | Mediterranean diet | |
| Other | herbal medicine | |
| Other | omega‐3 fatty acid supplementation | |
| Other | electronic data capture system | |
| Other | reflexology |
Six of the studies investigated physical activity (Bilberg 2005; Evans 2012; Hakkinen 2003; Harkcom 1985; Neuberger 2007 ‐ I; Wang 2008). The physical activity interventions included pool‐based therapy (Bilberg 2005), yoga (Evans 2012), dynamic strength training (Hakkinen 2003), stationary cycling (Harkcom 1985), low impact aerobics (Neuberger 2007 ‐ I) and Tai Chi (Wang 2008). Thirteen studies were broadly categorised as investigating psychosocial interventions (Danoff‐Burg 2006 ‐ I; Evers 2002; Furst 1987; Giraudet‐Le‐Quintrec 2007; Hammond 2008; Helliwell 1999; Hewlett 2011; Laforest 2008; Lorig 2005; Lorig 2008; Lumley 2011‐I; Riemsma 2003 ‐ I; Zangi 2012). These interventions included benefit finding (Danoff‐Burg 2006 ‐ I), expressive writing (Danoff‐Burg 2006 ‐ I; Lumley 2011‐I), cognitive behavioural therapy (Evers 2002; Hewlett 2011; Lumley 2011‐I), mindfulness (Zangi 2012), lifestyle management (Hammond 2008), energy conservation (Furst 1987), self‐management (Laforest 2008; Lorig 2005; Lorig 2008) and group education (Giraudet‐Le‐Quintrec 2007; Helliwell 1999; Riemsma 2003 ‐ I). The remaining five studies investigated a range of other non‐pharmacological interventions (Burgos 2009; Das Gupta 2009; Huffstutter 2007; Otter 2010; Skoldstam 2003).
Outcome measures
A wide range of self‐report measures were used to assess fatigue, with six of the 24 studies including two different self‐report fatigue measures (Danoff‐Burg 2006 ‐ I; Evans 2012; Furst 1987; Hewlett 2011; Neuberger 2007 ‐ I; Wang 2008). Thirteen studies used variations of a numerical rating scale (NRS) or visual analogue scale (VAS) to measure fatigue or tiredness (Danoff‐Burg 2006 ‐ I; Furst 1987; Hakkinen 2003; Hammond 2008; Hewlett 2011; Huffstutter 2007; Laforest 2008; Lorig 2005; Lorig 2008; Lumley 2011‐I; Riemsma 2003 ‐ I; Wang 2008; Zangi 2012). The majority of these studies used the VAS or NRS to measure average fatigue during a specific time period, for example the past seven days, although two studies monitored fatigue levels during a specific activity (Furst 1987; Hakkinen 2003). Seven studies used the Short Form 36 (SF‐36) vitality subscale to measure fatigue (Bilberg 2005; Burgos 2009; Das Gupta 2009; Evans 2012; Helliwell 1999; Skoldstam 2003; Wang 2008). Three studies used the Multidimensional Assessment of Fatigue (MAF) (Hewlett 2011; Neuberger 2007 ‐ I; Otter 2010), two studies used the Profile of Mood States (POMS) vigour subscale to monitor fatigue levels (Danoff‐Burg 2006 ‐ I; Neuberger 2007 ‐ I), two studies used the Functional Assessment of Chronic Illness Therapy – Fatigue (FACIT‐F) (Evans 2012; Giraudet‐Le‐Quintrec 2007), and one used the Checklist Individual Strength (CIS) (Evers 2002). The final study asked participants to rate their perception of change in fatigue from baseline using a four point Likert scale (Harkcom 1985).
Fatigue was identified as the single primary outcome in one study (Otter 2010) and fatigue impact was the single primary outcome in another study (Hewlett 2011). Burgos 2009 included tiredness as one of their three primary outcomes. Evers 2002 identified physical, psychological and social functioning as their primary outcomes, where physical functioning encompassed fatigue. None of the remaining studies reported fatigue as a primary outcome although six studies did not identify the primary outcome (Danoff‐Burg 2006 ‐ I; Das Gupta 2009; Evans 2012; Furst 1987; Harkcom 1985; Neuberger 2007 ‐ I).
Excluded studies
The 37 publications that were subsequently excluded did not meet the review inclusion criteria for the following reasons: 16 were not RCTs, 13 did not report fatigue as an outcome measure, seven did not report fatigue data separately for RA patients, and one paper was unobtainable. Details of the excluded studies can be found in the Characteristics of excluded studies table. A further two studies are awaiting classification, with one of the studies requiring translation (Wiesenauer 1991) and for the remaining study further data are needed before a decision can be made regarding inclusion (Berbert 2005). The additional seven studies identified through snowballing, which were retrieved in full and subsequently excluded, did not include fatigue as an outcome.
Risk of bias in included studies
Two authors independently reviewed all included studies for ‘risk of bias’ (Figure 2; Figure 3). Any discrepancies were easily resolved through group discussion. Eight items were assessed to determine ‘risk of bias’ although it should be noted that three of the eight items related to blinding (participants, personnel and outcome assessors). Only published material was used to assess risk of bias and authors were not contacted to seek clarification. Therefore, a number of items remained unclear and although it could not be stated that the quality criteria had been met it equally could not be stated that they had not been met.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Overall, two studies each met seven (Burgos 2009; Giraudet‐Le‐Quintrec 2007), and six (Hammond 2008; Lorig 2005) of the eight criteria. Five studies met five criteria (Danoff‐Burg 2006 ‐ I; Helliwell 1999; Hewlett 2011; Wang 2008; Zangi 2012) and a further three met four criteria (Bilberg 2005; Evers 2002; Otter 2010). Six studies only met three criteria (Evans 2012; Hakkinen 2003; Laforest 2008; Lorig 2008; Lumley 2011‐I; Neuberger 2007 ‐ I), two met two criteria (Furst 1987; Skoldstam 2003), two met one criterion (Harkcom 1985; Riemsma 2003 ‐ I) and the final two studies did not meet any of the criteria assessed (Das Gupta 2009; Huffstutter 2007).
Based upon intervention category, the studies investigating physical activity provided moderate quality evidence whereas the studies investigating psychosocial interventions provided low quality evidence. The remaining studies, categorised as 'other' interventions, were assessed as providing low quality evidence except for the study investigating a Mediterranean diet that was assessed as providing moderate quality evidence.
Allocation
There was poor reporting of the procedures used to conceal trial arm allocation with 14 of the 24 studies providing insufficient information to judge this criterion accurately (Bilberg 2005; Das Gupta 2009; Evans 2012; Evers 2002; Hakkinen 2003; Huffstutter 2007; Laforest 2008; Lorig 2005; Lorig 2008; Lumley 2011‐I; Neuberger 2007 ‐ I; Otter 2010; Riemsma 2003 ‐ I; Skoldstam 2003). Further to this, nine of the studies did not report sequence generation in sufficient detail (Danoff‐Burg 2006 ‐ I; Das Gupta 2009; Evans 2012; Hakkinen 2003; Harkcom 1985; Huffstutter 2007; Lorig 2008; Otter 2010; Riemsma 2003 ‐ I). The remaining studies described a variety of acceptable methods for sequence generation and allocation concealment. In the majority of the latter studies the methods for developing an 'a priori' list for randomisation were described and pre‐prepared sealed, opaque, sequentially numbered envelopes were the favoured method of allocation concealment.
Based upon intervention category, three of the six physical activity intervention studies identified appropriate random sequence allocation (Bilberg 2005; Neuberger 2007 ‐ I; Wang 2008) and two appropriately concealed allocation (Harkcom 1985; Wang 2008). Ten of the 13 psychosocial intervention studies identified appropriate random sequence allocation (Evers 2002; Furst 1987; Giraudet‐Le‐Quintrec 2007; Hammond 2008; Helliwell 1999; Hewlett 2011; Laforest 2008; Lorig 2005; Lumley 2011‐I; Zangi 2012) and seven appropriately concealed allocation (Danoff‐Burg 2006 ‐ I; Furst 1987; Giraudet‐Le‐Quintrec 2007; Hammond 2008; Helliwell 1999; Hewlett 2011; Zangi 2012). For the remaining five studies only two appropriately identified random sequence allocation (Burgos 2009; Skoldstam 2003) and only one detailed allocation concealment adequately (Burgos 2009).
Blinding
Blinding was a limitation for the large majority of the studies. Nine studies failed to blind participants (Das Gupta 2009; Hammond 2008; Hewlett 2011; Huffstutter 2007; Laforest 2008; Lorig 2008; Neuberger 2007 ‐ I; Otter 2010; Zangi 2012) and a further 10 studies failed to adequately report blinding of participants (Bilberg 2005; Evers 2002; Furst 1987; Hakkinen 2003; Harkcom 1985; Helliwell 1999; Lumley 2011‐I; Riemsma 2003 ‐ I; Skoldstam 2003; Wang 2008). Fifteen studies did not blind the study personnel (Danoff‐Burg 2006 ‐ I; Das Gupta 2009; Evans 2012; Evers 2002; Giraudet‐Le‐Quintrec 2007; Hammond 2008; Harkcom 1985; Helliwell 1999; Hewlett 2011; Huffstutter 2007; Laforest 2008; Lorig 2008; Neuberger 2007 ‐ I; Skoldstam 2003; Zangi 2012) and a further six failed to report the procedure for this (Bilberg 2005; Furst 1987; Hakkinen 2003; Lumley 2011‐I; Riemsma 2003 ‐ I; Wang 2008). Two studies did not blind the outcome assessors (Huffstutter 2007; Skoldstam 2003) and 10 studies did not report this adequately (Burgos 2009; Das Gupta 2009; Evans 2012; Evers 2002; Furst 1987; Hakkinen 2003; Harkcom 1985; Lorig 2008; Lumley 2011‐I; Riemsma 2003 ‐ I). Several studies acknowledged the difficulties associated with blinding participants to non‐pharmacological interventions and made attempts to blind the outcome assessor by using personnel not otherwise involved in the study. However, several of the studies used subjectively‐reported outcomes with unblinded participants. In this situation the use of a blinded outcome assessor would not have changed the risk of bias.
All physical activity intervention studies and those categorised as 'other' either did not blind adequately or provided insufficient information. Only one of the psychosocial intervention studies provided adequate blinding (Lorig 2005).
Incomplete outcome data
The majority of studies provided complete outcome data with only four studies assessed as providing incomplete data (Das Gupta 2009; Furst 1987; Harkcom 1985; Huffstutter 2007) and a further four studies judged to be unclear (Danoff‐Burg 2006 ‐ I; Laforest 2008; Riemsma 2003 ‐ I; Skoldstam 2003). The four studies that were considered to have incomplete outcome data all failed to explain how missing data were handled. The reasons for participants leaving the study early were also omitted in some studies. The studies that met this criterion mainly performed analysis on an intention‐to‐treat basis although the methods used varied.
Five of the six physical activity intervention studies were considered to be at low risk of incomplete outcome data reporting, the remaining study was considered to be at high risk (Harkcom 1985). For the psychosocial intervention studies, nine were considered to be at low risk, one at high risk (Furst 1987) and three were unclear for incomplete outcome data reporting (Danoff‐Burg 2006 ‐ I; Laforest 2008; Riemsma 2003 ‐ I). For the five remaining studies, two were at low risk, one was unclear (Skoldstam 2003) and two at high risk (Das Gupta 2009; Huffstutter 2007).
Selective reporting
The majority of studies were judged to be free from selective reporting with only four studies considered to have selectively reported the findings (Das Gupta 2009; Furst 1987; Harkcom 1985; Neuberger 2007 ‐ I) and two studies were judged to be unclear (Huffstutter 2007; Lumley 2011‐I). One study reported the findings of an outcome that was not included within the methodology (Das Gupta 2009) and a further study combined the outcomes of different intervention groups resulting in insufficient detail (Harkcom 1985). Three studies did not report the results for all the outcomes listed in the methodology although the authors for one of these studies subsequently provided these data upon request.
For the physical activity intervention studies, two were considered to be at high risk of selective reporting (Harkcom 1985; Neuberger 2007 ‐ I) and the remaining four at low risk. For the psychosocial intervention studies, 11 were considered to be at low risk of selective reporting, one was unclear (Lumley 2011‐I) with the one remaining study considered to be at high risk (Furst 1987). For the remaining five studies, three were at low risk, one unclear (Huffstutter 2007) and one at high risk (Das Gupta 2009) of selective reporting.
Other potential sources of bias
Thirteen of the 24 studies were considered to be at high risk of bias for ‘other’ reasons (Bilberg 2005; Das Gupta 2009; Evans 2012; Furst 1987; Harkcom 1985; Helliwell 1999; Laforest 2008; Lorig 2008; Neuberger 2007 ‐ II; Otter 2010; Skoldstam 2003; Wang 2008; Zangi 2012). The main reasons identified were study arms being unbalanced at baseline, a risk of contamination between the arms, payment of participants in one arm of the study, and control arm participants advised that they would be entitled to receive the active intervention at the end of the study period.
For the physical activity intervention studies, five were considered to be at high risk of other bias (Bilberg 2005; Evans 2012; Harkcom 1985; Neuberger 2007 ‐ I; Wang 2008) and the remaining study at low risk. For the psychosocial intervention studies, seven were considered to be at low risk of other bias, one unclear (Riemsma 2003 ‐ I) and five at high risk (Furst 1987; Helliwell 1999; Laforest 2008; Lorig 2008; Zangi 2012). For the remaining five studies, three were at high risk of selective reporting (Das Gupta 2009; Otter 2010; Skoldstam 2003) and one was unclear (Huffstutter 2007).
Effects of interventions
Fatigue
It was not considered appropriate to combine the data for all the studies included within the review due to the heterogeneity in relation to the interventions under investigation. Data were therefore combined for subgroups, in separate meta‐analyses, for studies investigating physical activity interventions and psychosocial interventions. The remaining five studies did not fit within these subgroups and were therefore reported narratively.
Physical activity interventions: effect on fatigue
A meta‐analysis was used to combine the mean change scores from pre‐ to post‐test for the six studies investigating physical activity interventions (see Analysis 1.1). There were a maximum of seven comparisons possible due to the inclusion of two interventions in one study (Neuberger 2007 ‐ I). However, mean change data for fatigue were not available for one of the seven comparisons (Harkcom 1985). The remaining six comparisons provided data for 219 participants who received a physical activity intervention and 152 participants in the control arm. Data were combined using a random‐effects model meta‐analysis due to the heterogeneity within the outcome measures used to assess fatigue. At the end of the intervention period physical activity was statistically significantly more effective than the control (SMD ‐0.36, 95% CI ‐0.62 to ‐0.10; number needed to treat for an additional beneficial outcome (NNTB) 7, 95% CI 4 to 26), demonstrating a small effect.
The quality of the evidence was graded as moderate using the GRADE approach (see summary of findings Table for the main comparison). The funnel plot did not demonstrate obvious publication bias for the physical activity interventions although it cannot be ruled out (see Figure 4).
Funnel plot of comparison: 1 Physical activity versus control, outcome: 1.1 Fatigue.
Psychosocial interventions: effect on fatigue
A meta‐analysis was used to combine the mean change scores from pre‐ to post‐test for the 13 studies investigating psychosocial interventions (see Analysis 2.1). There were a maximum of 16 comparisons possible due to the inclusion of two intervention arms in three studies (Danoff‐Burg 2006 ‐ I; Lumley 2011‐I; Riemsma 2003). However, mean change data for fatigue were not available for one of the comparisons (Furst 1987). The remaining 15 comparisons provided data for 843 participants who received a psychosocial intervention and 713 participants in the control arm. Data were combined using a random‐effects model meta‐analysis due to the heterogeneity within the outcome measures used to assess fatigue. At the end of the intervention period psychosocial interventions were statistically significantly more effective than the controls (SMD ‐0.24, 95% CI ‐0.40 to ‐0.07; NNTB 9, 95% CI 6 to 33), demonstrating a small effect.
The quality of the evidence was graded as low using the GRADE approach (see summary of findings Table for the main comparison).The funnel plot did not demonstrate obvious publication bias for the psychosocial interventions although it cannot be ruled out (see Figure 5).
Funnel plot of comparison: 2 Psychosocial versus control, outcome: 2.1 Fatigue.
Other interventions: effect on fatigue
The remaining five studies investigated diverse non‐pharmacological interventions and were therefore not appropriate for combining within a meta‐analysis. In brief, Skoldstam 2003 investigated Mediterranean diet compared to an ordinary Western diet. The Mediterranean diet arm demonstrated statistically significant improvement in the SF‐36 vitality score at the end of the intervention (12 weeks) whereas no statistically significant change was shown in the Western diet arm; between arm comparisons were not reported (see Analysis 3.1). Burgos 2009 investigated the herbal medicine Andrographis paniculata compared to a placebo. No statistically significant differences were reported between arms for tiredness measured on a VAS (see Analysis 4.1). Das Gupta 2009 investigated omega‐3 fatty acid supplementation in patients receiving indomethacin. Both study arms demonstrated statistically significant improvements in SF‐36 vitality between baseline and at 12 weeks, with between arm comparisons not reported (see Analysis 5.1). Huffstutter 2007 investigated the use of a data capture system to provide patients with graphical summarised health information in comparison to a usual care control arm. Statistical analysis of VAS fatigue data was not reported. Additional data provided by the authors demonstrated small improvements in VAS fatigue from baseline to follow‐up in both arms (see Analysis 6.1). Finally, Otter 2010 investigated reflexology compared to a non‐specific foot massage with fatigue as the primary outcome. The authors reported a greater mean reduction in fatigue in the reflexology arm compared to the control arm but did not perform inferential statistics on the data due to the small number of participants (see Analysis 7.1).
Pain
Two of the 24 studies did not include pain as an outcome (Bilberg 2005; Giraudet‐Le‐Quintrec 2007). Fourteen of the studies that measured pain used variations of a VAS or NRS (Burgos 2009; Danoff‐Burg 2006 ‐ I; Das Gupta 2009; Furst 1987; Hakkinen 2003; Hammond 2008; Hewlett 2011; Huffstutter 2007; Laforest 2008; Lorig 2005; Lorig 2008; Skoldstam 2003; Wang 2008; Zangi 2012). Other measures used were a Likert scale (Harkcom 1985); the short‐form McGill Pain Questionnaire (Neuberger 2007 ‐ I), the pain subscale of the Dutch AIMS2 (Riemsma 2003 ‐ I; Lumley 2011‐I); the pain scale of the Impact of Rheumatic Diseases on General Health and Lifestyle (IRGL) (Evers 2002), the Pain Disability Index (Evans 2012), the Bodily Pain subscale of the SF‐36 (Helliwell 1999) and the Manchester Foot Pain Disability Questionnaire (Otter 2010).
For the studies investigating physical activity interventions, Harkcom 1985 reported improvements in pain over time for the exercise programme in comparison to home‐based exercise or a control arm. However, statistical analysis was not reported separately for the pain data. Hakkinen 2003 reported a statistically significant improvement in average pain intensity at 24 months in the dynamic strength training arm compared to a control arm that carried out range of motion and stretching exercises. The remaining physical activity intervention studies that recorded pain as an outcome reported no statistically significant effects (Evans 2012; Wang 2008).
Six of the psychosocial intervention studies that measured pain as an outcome did not report separate RA data (Danoff‐Burg 2006 ‐ I; Hammond 2008; Laforest 2008; Lorig 2005; Lorig 2008; Zangi 2012). Four of the studies reported no statistically significant effects either over time or between arms (Evers 2002; Helliwell 1999; Hewlett 2011; Riemsma 2003 ‐ I). One study reported statistically significant improvement in pain over time but no statistically significant differences between the intervention and control arms (Furst 1987). The final study reported a statistically significant improvement in pain following a coping skills training intervention compared to the control education arm but no statistically significant difference between the written emotional disclosure arm and control writing arm (Lumley 2011‐I).
For the 'other' categorised interventions, Otter 2010 reported a decrease in pain for both study arms but no inferential statistics were carried out. One study reported no statistically significant effects either over time or between arms (Burgos 2009). Two of the studies reported statistically significant improvement in pain over time but no statistically significant differences between the intervention and control arms (Das Gupta 2009; Huffstutter 2007). Finally, Skoldstam 2003 reported a statistically significant reduction in pain following a 12‐week Mediterranean diet intervention in comparison to a usual diet.
Anxiety
Only seven of the 24 studies included anxiety as an outcome (Danoff‐Burg 2006 ‐ I; Evans 2012; Evers 2002; Giraudet‐Le‐Quintrec 2007; Hewlett 2011; Lumley 2011‐I; Zangi 2012) with a range of different assessment methods. Six of the seven studies were categorised as psychosocial interventions. One of these did not provide data specific to the RA participants (Zangi 2012) and a further study did not report the findings for anxiety within the results (Lumley 2011‐I). Danoff‐Burg 2006 ‐ I only measured anxiety at baseline but interestingly reported that higher levels of anxiety were statistically significantly associated with greater fatigue at both one and three months (combined data for participants with RA and systemic lupus erythematosus (SLE)). Giraudet‐Le‐Quintrec 2007 and Hewlett 2011 reported no statistically significant changes in anxiety due to their psychosocial interventions. Evers 2002 also reported no condition by time interaction for anxiety in their investigation of a cognitive behavioural therapy programme. The final study that investigated the effect of Ivengar yoga reported no statistically significant effect for anxiety (Evans 2012).
Depression
Ten studies included depression as an outcome (Danoff‐Burg 2006 ‐ I; Evans 2012; Evers 2002; Giraudet‐Le‐Quintrec 2007; Hewlett 2011; Laforest 2008; Lumley 2011‐I; Neuberger 2007 ‐ I; Wang 2008; Zangi 2012) with the Centre for Epidemiological Studies depression scale (CES‐D) being used in four of the 10 studies. Two of the studies did not provide full outcome data or an analysis for the depression data (Laforest 2008; Lumley 2011‐I) and a further two studies only provided combined data for participants with inflammatory arthritis (Danoff‐Burg 2006 ‐ I; Zangi 2012).
For physical activity interventions, Neuberger 2007 ‐ I reported an overall positive effect for depression but results for univariate analysis were not reported. Wang 2008 reported a decrease in depression immediately following a 12‐week Tai Chi programme with a corresponding increase in depression in the control arm and an overall statistically significant between arm effect. Evans 2012 reported that there was no statistically significant effect due to an Ivengar yoga intervention compared to a control arm.
For psychosocial interventions, one study reported no statistically significant effects in relation to depression (Giraudet‐Le‐Quintrec 2007). Evers 2002 and Hewlett 2011 reported that depression was statistically significantly reduced following a cognitive behavioural therapy intervention in comparison to the control arms.
Disability
Eighteen of the 24 studies included disability as an outcome measure. Sixteen of the 18 studies used the Health Assessment Questionnaire (HAQ) or a modified version of the HAQ to assess disability. The remaining studies used the Mobility and Self‐care scales of the Impact of Rheumatic Diseases on General Health and Lifestyle to assess disability (Evers 2002) or the Arthritis Impact Measurement Scales 2 (AIMS2) physical disability subscale Lumley 2011‐I).
Four of the six studies categorised as physical activity studies included disability as an outcome. The studies investigating hydrotherapy (Bilberg 2005) and Tai Chi (Wang 2008) demonstrated statistically significant improvements in the intervention arm compared to the control arm between baseline and follow‐up. The studies investigating strength training (Hakkinen 2003) and Ivengar yoga (Evans 2012) did not demonstrate a statistically significant difference between study arms.
Ten of the 13 studies investigating psychosocial interventions included disability as an outcome measure although four of these did not provide separate RA data (Danoff‐Burg 2006 ‐ I; Hammond 2008; Lorig 2005; Lorig 2008). Four of the six remaining studies reported no statistically significant time by arm interaction (Evers 2002; Giraudet‐Le‐Quintrec 2007; Helliwell 1999; Lumley 2011‐I). One study (Furst 1987) did not carry out statistical analysis of the disability data but reported that there were no differences between the arms over time. The final study reported statistically significantly better disability in the trial arm that had received cognitive behavioural therapy compared to the control arm at the primary endpoint (Hewlett 2011).
In the remaining studies, Burgos 2009 reported a statistically significant improvement in disability over time with no statistically significant differences between the arm receiving andrographolides and the placebo arm. Skoldstam 2003 reported a statistically significant difference between arms from baseline to the 12‐week follow‐up. Findings were in favour of the intervention arm receiving the Mediterranean diet. Finally, Das Gupta 2009 and Huffstutter 2007 did not present the findings for disability despite including the HAQ as an outcome measure within the methods.
Tender and swollen joints
Several studies included the Disease Activity Score (DAS28) as an outcome. This outcome incorporates an assessment of the number of tender and swollen joints. However, the separate scores were often not reported. Studies were only reported here that provided separate evaluation of tender or swollen joints, or both, or results for the Ritchie Articular Index (a graded assessment of 26 joint regions to assess tenderness plus a 44 joint count to assess swelling). Ten of the 19 studies met these criteria.
Four of the studies investigating physical activity interventions reported findings for tender and swollen joints. Harkcom 1985 reported statistically significant reductions in joint counts (combined tenderness and swelling scores) in all three cycle ergometry intervention arms between baseline and post‐treatment, with a statistically non‐significant reduction in the control arm. However, statistical analysis was not reported for between arm comparisons. Hakkinen 2003 reported improvements in the Ritchie Articular Index (RAI) in both the strength training arm and the control arm with no statistically significant differences between arms. Neuberger 2007 ‐ I reported no statistically significant differences in total joint count between the low impact aerobic exercise arms and the control arm. Similarly, Wang 2008 reported no statistically significant differences between the hydrotherapy arm and control arm in relation to joint pain, joint swelling or RAI values.
Only two of the studies investigating psychosocial interventions measured and reported tender and swollen joint counts. Furst 1987 reported a statistically non‐significant increase in RAI (worse) in both the energy conservation arm and the control. Between arm statistical analysis was not however reported. Helliwell 1999 reported no statistically significant difference in RAI between patients receiving group education and a control.
In the remaining studies, Burgos 2009 reported no statistically significant difference in tender joint counts, swollen joint counts, grade of swollen joints or grade of tender joints between the herbal medicine and control arm from baseline to follow‐up. Das Gupta 2009 reported that tender and swollen joint counts decreased statistically significantly in the arm receiving omega‐3 fatty acids as well as the placebo control arm. Between arm statistical analysis was not reported. Huffstutter 2007 reported a statistically significant improvement in mean painful joint count in the arm receiving health tracker data compared to a statistically non‐significant improvement in the control arm. Again, between trial arm statistical analysis was not reported. Finally, Skoldstam 2003 demonstrated a statistically significant decrease in swollen joint count over time in the trial arm receiving a Mediterranean diet compared to the control arm. There was no corresponding difference in tender joint counts.
Adverse events
No adverse events were reported in 21 of the 24 studies. However, in some cases it was not clear if this was due to the absence of any adverse events or poor reporting. The remaining three studies reported adverse events (Burgos 2009; Huffstutter 2007; Skoldstam 2003) but none were serious and there was no clear difference in the incidence or severity of the adverse events between the intervention and control arms. No adverse effects or side effects were reported in any of the studies.
Discussion
Summary of main results
The aim of this review was to provide an overview of the benefits and harms of non‐pharmacological interventions for fatigue in people with RA. The review revealed 24 studies in which a non‐pharmacological intervention had been investigated in an RCT design and fatigue had been included as an outcome measure. The interventions were heterogenous with six studies investigating a form of physical activity, 13 investigating a psychosocial intervention, and the five remaining studies investigating a herbal medicine, Mediterranean diet, omega‐3 fatty acid supplementation, reflexology and the provision of health tracker information. The quality of the evidence varied from low to moderate.
Overall completeness and applicability of evidence
One study identified fatigue as the single primary outcome and a further study identified fatigue impact as a the primary outcome. Tiredness was also identified as the primary outcome in one study and a further study included fatigue as one of several primary outcomes. As a consequence the primary purpose of the interventions for the majority of studies was not fatigue reduction and there was little or no apparent consideration of fatigue mechanisms in the design of the interventions. Future research needs to focus specifically upon fatigue to determine the most effective methods for management. Interventions should also be designed with consideration given to potential causal pathways and mechanisms of fatigue. The lack of specific focus on fatigue within the included studies may have resulted in an underestimation of the effectiveness of non‐pharmacological interventions. It should be noted that only one of the studies identified the presence of fatigue as a specific inclusion criteria. It is highly likely that for some participants fatigue was not a clinically significant problem thus reducing the potential for improvement. Future research therefore needs to be undertaken with fatigued participants. Further to this, only one of the included studies was specifically powered to detect a change in fatigue, although it is likely that some studies did have sufficient numbers for this purpose. It is possible that fatigue has been included as a secondary outcome in additional studies and not reported where no effect was detected. This potential for selective reporting may have led to an exaggeration in the benefits of the included interventions upon fatigue. The absence of reporting of adverse events or side effects does not allow the important benefits to be balanced against potential harms.
Quality of the evidence
Fatigue outcome measures need to be standardised in future RA research. Although 13 of the included studies used a NRS or VAS there was no standardisation of the root question or anchor statements. A range of other multi‐dimensional fatigue measures were used that have not been validated in full for use in RA, for example, the FACIT‐F, MAF and CIS (Hewlett 2011b). The use of the SF‐36 may also be questionable as vitality may not be at the opposite end of the spectrum to fatigue. Consistent use of outcomes would simplify pooling of data and allow comparison between interventions.
Due to inadequate reporting in the majority of included studies it was often not possible to determine whether the quality criteria had been met. This resulted in a large number of items being scored as unclear rather than met or not met. Blinding was highlighted as a limitation in the majority of the included studies. There are inherent difficulties in blinding non‐pharmacological interventions, although it is not impossible and future research needs to make efforts to address this to limit risk of bias.
Potential biases in the review process
The inclusion criteria for this review were intentionally broad to capture all non‐pharmacological interventions that may have potential to reduce fatigue in patients with RA. Unsurprisingly this resulted in heterogeneity between the interventions under investigation. For the purpose of data pooling an artificial cut off was created between psychosocial and physical activity interventions. In general it was clear where the main component of the intervention was physical activity or psychosocial, however, there was also some overlap in a few studies. In the future, assuming that the number and quality of studies increases, it may be possible to determine a priori meta‐analysis with more homogenous interventions. It may also be possible to perform meta‐analysis upon intervention subgroups; for example, physical activity interventions may be classified as primarily aerobic training or resistance training. This would help to create consensus in relation to optimal management of fatigue and better informed clinical guidelines.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Funnel plot of comparison: 1 Physical activity versus control, outcome: 1.1 Fatigue.
Funnel plot of comparison: 2 Psychosocial versus control, outcome: 2.1 Fatigue.
Comparison 1 Physical activity versus control, Outcome 1 Fatigue.
Comparison 2 Psychosocial versus control, Outcome 1 Fatigue.
Comparison 3 Mediterranean diet versus control, Outcome 1 Fatigue.
Comparison 4 Andrographis paniculata versus control, Outcome 1 Fatigue.
Comparison 5 Omega‐3 fatty acid versus control, Outcome 1 Fatigue.
Comparison 6 Data tracker versus control, Outcome 1 Fatigue.
Comparison 7 Reflexology versus control, Outcome 1 Fatigue.
| Non‐pharmacological interventions for rheumatoid arthritis | ||||||
| Patient or population: patients with rheumatoid arthritis | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | No of Participants | Quality of the evidence | Comments (95% CI) | |
| Assumed risk | Corresponding risk | |||||
| Control | Non‐Pharmacological Interventions | |||||
| fatigue (physical activity interventions) | The mean fatigue in the control groups was | The mean fatigue (physical activity interventions) in the intervention groups was | 371 | ⊕⊕⊕⊝ | SMD ‐0.36 (‐0.62 to ‐0.10) Relative percent change ‐13.7% (‐23.6 to ‐3.8) NNTB 7 (4 to 26) | |
| fatigue (psychosocial interventions) | The mean fatigue in the control groups was | The mean fatigue (psychosocial interventions) in the intervention groups was | 1,556 | ⊕⊕⊝⊝ | SMD ‐0.24 (‐0.40 to ‐0.07) Relative percent change ‐9.1% (‐15.2 to ‐2.7) NNTB 10 (6 to 33) | |
| fatigue (Andrographis paniculata) | The mean fatigue in the control groups was | The mean fatigue (Andrographis Paniculata) in the intervention groups was | 58 | ⊕⊕⊝⊝ | SMD ‐0.25 (‐0.77 to 0.27) Relative percent change ‐9.5% (‐29.3 to 10.3) NNTB not applicable | |
| fatigue (data tracker) | The mean fatigue in the control groups was | The mean fatigue (data tracker) in the intervention groups was | 714 | ⊕⊕⊝⊝ | SMD 0.06 (‐0.10 to 0.21) Relative percent change 2.3% (‐3.8 to 8.0) NNTB not applicable | |
| fatigue (Omega‐3 Fatty acids) | The mean fatigue in the control groups was | The mean fatigue (Omega‐3 Fatty acids) in the intervention groups was | 81 | ⊕⊕⊝⊝ | SMD 0.93 (0.47 to 1.39) Relative percent change 35.4% (17.9 to 53.0) NNTB not applicable | |
| fatigue (Mediterranean diet) | The mean fatigue in the control groups was | The mean fatigue (Mediterranean diet) in the intervention groups was | 51 | ⊕⊕⊕⊝ | SMD 0.37 (‐0.18 to 0.93) Relative percent change 14.1% (‐6.9 to 35.4) NNTB not applicable | |
| fatigue (reflexology) | The mean fatigue in the control group was 6.3 VAS (score: 0‐10) | The mean fatigue (Reflexolgy) in the intervention groups was | 11 (1 study) | ⊕⊕⊝⊝ | SMD ‐1.24 (‐2.59 to 0.11) Relative percent change ‐47.2% (‐98.7 to 4.2) NNTB not applicable | |
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1 A lower score means less fatigue 2 Based on a conversion from Hewlett S et al (Mean: 6.3, SD: 2.4). | ||||||
| Study ID | Intervention category | Specific intervention |
| Physical activity | pool‐based therapy | |
| Physical activity | Yoga | |
| Physical activity | strength training | |
| Physical activity | stationary cycling | |
| Physical activity | aerobic exercise | |
| Physical activity | Tai Chi | |
| Psychosocial | benefit finding and expressive writing | |
| Psychosocial | cognitive skills training & written emotional disclosure | |
| Psychosocial | cognitive behavioural therapy | |
| Psychosocial | cognitive behavioural therapy | |
| Psychosocial | mindfulness based group intervention | |
| Psychosocial | lifestyle management | |
| Psychosocial | education incorporating energy conservation | |
| Psychosocial | education incorporating self management | |
| Psychosocial | education incorporating self management | |
| Psychosocial | education incorporating self management | |
| Psychosocial | group education | |
| Psychosocial | group education | |
| Psychosocial | group education | |
| Other | Mediterranean diet | |
| Other | herbal medicine | |
| Other | omega‐3 fatty acid supplementation | |
| Other | electronic data capture system | |
| Other | reflexology |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 6 | 371 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.36 [‐0.62, ‐0.10] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 15 | 1556 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.24 [‐0.40, ‐0.07] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 1 | 51 | Std. Mean Difference (IV, Random, 95% CI) | 0.37 [‐0.18, 0.93] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 1 | 58 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.25 [‐0.77, 0.27] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 1 | 81 | Std. Mean Difference (IV, Random, 95% CI) | 0.93 [0.47, 1.39] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 1 | 714 | Std. Mean Difference (IV, Random, 95% CI) | 0.06 [‐0.10, 0.21] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Fatigue Show forest plot | 1 | 11 | Std. Mean Difference (IV, Random, 95% CI) | ‐1.24 [‐2.59, 0.11] |
