Abstract
Mind-body interventions to manage stress-related health problems are of widespread interest. One of the best known methods is mindfulness-based stress reduction (MBSR), and MBSR courses are now offered by health services, as well as in social and welfare settings. In this systematic review, we report on the effects of MBSR interventions on health, quality of life, and social functioning. From the more than 3,000 potentially relevant references identified in two extensive searches, we included 31 relevant studies with an overall total of 1,942 participants, each of whom had been randomised to receive MBSR or other treatment strategies (most often a waiting list control).
We utilised all outcome data published in the selected studies using a new statistical method for calculating the effect size. This method addressed the problems presented by the interdependence of many measurements of outcomes. 26 of the 31 studies were identified as having data suitable for meta-analysis.
MBSR was found to have a moderate and consistent positive effect on mental health outcomes in both patients selected with somatic problems and with mild to moderate psychological problems, and among participants recruited from community settings. MBSR interventions improved outcomes measuring different aspects of personal development and quality of life. The effects on somatic health outcomes were somewhat smaller. No adverse effects were described. Few studies were found that evaluated the impact of MBSR on social functioning, such as the ability to work.
Key messages
Mind-body interventions to manage stress-related health problems are of widespread interest. One of the best known methods is mindfulness-based stress reduction (MBSR), and MBSR courses are now offered by health services, as well as in social and welfare settings. In this systematic review, we report on the effects of MBSR interventions on health, quality of life, and social functioning. From the more than 3,000 potentially relevant references identified in two extensive searches, we included 31 relevant studies with an overall total of 1,942 participants, each of whom had been randomised to receive MBSR or other treatment strategies (most often a waiting list control). We utilised all outcome data published in the selected studies using a new statistical method for calculating the effect size. This method addressed the problems presented by the interdependence of many measurements of outcomes.
26 of the 31 studies were identified as having data suitable for meta-analysis. MBSR was found to have a moderate and consistent positive effect on mental health outcomes in both patients selected with somatic problems and with mild to moderate psychological problems, and among participants recruited from community settings. MBSR interventions improved outcomes measuring different aspects of personal development and quality of life. The effects on somatic health outcomes were somewhat smaller. No adverse effects were described. Few studies were found that evaluated the impact of MBSR on social functioning, such as the ability to work.
Executive summary/Abstract
BACKGROUND
Stress and distress are common experiences central to many of the problems occupying health and social services and efforts to improve both health and quality of life are receiving increasing attention. Evaluative research on mind-body interventions is also growing and one of the best studied efforts to reduce stress is mindfulness-based stress reduction (MBSR). Developed by Kabat-Zinn in 1979, MBSR is based on old spiritual traditions and includes regular meditation. Mindfulness is a way of intentionally attending to the present moment in a non-judgemental way. A number of reviews and meta-analyses on MBSR have been conducted, but few have adhered to the meta-analytic protocol stipulated by the Cochrane and Campbell collaborations. The last review of all relevant target groups was published in 2004.
OBJECTIVES
To evaluate the effect of mindfulness-based stress reduction (MBSR) on health, quality of life, and social functioning in adults.
SEARCH STRATEGY
We searched all relevant databases: MEDLINE, AMED, PsycINFO, EMBASE, Ovid Nursing Full Text Plus, the British Nursing Index and Archive, the Cochrane Central Register of Controlled Trials (CENTRAL), SIGLE, Web of Science®, SveMed+, Dissertation Abstracts International, ERIC, Social Services Abstracts, Sociological Abstracts, the International Bibliography of Social Sciences, and ProQuest. The searches were conducted in July 2008 and again in September 2010.
SELECTION CRITERIA
Randomised controlled trials on all target groups were included where the intervention followed the MBSR protocol developed by Kabat-Zinn, allowing for variations in the length of the MBSR courses. We accepted all types of control groups and no language restrictions were imposed.
DATA COLLECTION AND ANALYSIS
Two reviewers independently read the titles, retrieved the studies, and extracted data from all the included studies. We calculated standardised mean differences (expressed as Hedges' g-values) from all of the study outcomes using Comprehensive Meta Analysis. The meta-analyses were undertaken using the Metafor Package which is part of the statistical program ‘R’; we used a newly developed technique (Robust Standard Errors) to address the statistical challenge presented by clusters of internally correlated effect estimates.
RESULTS
We identified 31 RCTs with an overall total of 1,942 participants. Seven studies included people with mild to moderate psychological problems, 13 studies targeted people with various somatic conditions, and 11 studies recruited people from the general population. 26 of the 31 RCTs were used for the meta-analyses (an overall total of 1,456 persons). All effect sizes are expressed using Hedges' g-values, and positive values indicate beneficial effects. Post-intervention effect sizes were as follows: for measures of anxiety 0.53 (95% CI 0.43, 0.63), for depression 0.54 (95% CI 0.35, 0.74), and for stress/distress 0.56 (95% CI 0.44, 0.67). The overall effect size post-intervention for the combined outcome ‘mental health’ was 0.53 (95% CI -0.43, 0.64). Heterogeneity was low and tau square-values (for between-study variance) ranged from 0 to 0.03. The results for measures of personal development were 0.50 (95% CI 0.35, 0.66), quality of life 0.57 (95% CI 0.17, 0.96), mindfulness 0.70 (95% CI 0.05, 1.34), and somatic health 0.31 (95% CI 0.10, 0.52). Results for quality of life and mindfulness showed moderate to large heterogeneity.
Effect sizes for the combined mental health outcomes were relatively similar across the range of target groups: 0.50 for clinical and 0.62 for non-clinical populations and this difference is not significant. Likewise the effect size was 0.51 both for people recruited because of a somatic condition and for those with a mental health problem. Effect sizes for mental health were not particularly influenced by the length of intervention, self-reported practice, risk of bias, or whether analyses were done as intention to treat or per protocol, but they were positively correlated with course attendance. Only nine studies included follow-up data; the effects diminished over time except in one study in which refresher classes were held. Very little data were found on social functioning, and no information at all on side effects and costs.
AUTHORS' CONCLUSIONS
MBSR has a moderate and consistent effect on a number of measures of mental health for a wide range of target groups. It also appears to improve measures of personal development such as empathy and coping, and enhance both mindfulness, quality of life and improve some aspects of somatic health. Hardly any included studies measured either social function or work ability. There is a paucity of data on long-term effects.
1 Background
1.1 DESCRIPTION OF THE CONDITION
Stress is ubiquitous in modern life. While some people are prompted to respond positively to it, more often than not it exerts a negative influence. At its worst, stress destroys lives. The demands of life are external but stress is generated from within and stressors may be real or imagined. How we handle situations, persons and emotions — in other words, how we become stressed or manage to keep calm — is central to staying healthy, coping with illness and enjoying life. These are skills that can be practised and exercised.
Prevalence rates for distress and mild to moderate psychological problems are high among children, adolescents and adults, and associated chronic musculoskeletal pain is common. While our understanding of such widespread problems is limited, we do know that stress is probably both a cause and a consequence of them.
Stress is also part of our everyday working life. In a series of surveys undertaken at five year intervals in the European Union, stress was identified as the second most common threat posed by working environments and an issue affecting a fifth of the workforce at any time (European Risk Observatory, 2009). Stress can lead to an increased risk of disease, including cardiovascular disease (Cohen, 2007; Chandola, 2008). Likewise there is mounting evidence that stress caused by traumatic life events increases the risk of chronic somatic and psychological problems affecting health and quality of life (McEwen, 2008); adverse childhood experiences are especially harmful (Brown, 2009).
1.2 DESCRIPTION OF THE INTERVENTION
Mindfulness-Based Stress Reduction, or MBSR, is a well described group-based mind-body intervention programme that has received considerable research attention (Kabat-Zinn 1990). ‘Mindfulness' may be defined as the ability to non-judgementally observe sensations, thoughts, emotions, and the environment while, at the same time, encouraging openness, curiosity and acceptance. An MBSR programme to develop and strengthen this skill was developed by the University of Massachusetts Medical Center in 1979 as an intervention designed to relieve stress and help people cope with illness. This programme is now offered at several hundred healthcare institutions in the USA and Europe (Santorelli, 1999). Target groups include people with chronic physical pain, illnesses such as cancer, or mental illnesses, including anxiety, depression or burnout. In addition, the programme has been applied to non-clinical populations, including students, therapists and prison inmates.
The standard MBSR mindfulness training is an eight week group programme with weekly sessions of between 2-2 ½ hours and an all-day session in the last two weeks. Shorter weekly sessions (30-90 minutes) may be offered as an alternative, and some programmes omit the all day session entirely. Weekly sessions include mental and physical mindfulness exercises as standardised core elements. These include: body scan exercises in which ‘neutral attention’ is directed towards sensations from the different parts of the body when sitting or lying still (in other words, participants observe these sensations without trying to achieve any particular objective); mental exercises focusing attention on breathing; physical exercises focussing on an awareness of bodily sensations; and practising being fully aware during everyday activities by using breathing as an anchor for attention. Essential to all parts of the programme is the development of an accepting and non-reactive attitude to what one experiences in each moment. The intervention is rooted in ancient Buddhist Vipassana (‘insight’) and Shamatha (‘focussed’) meditation and yoga exercises. However, it is free from religious purpose or affiliation and is described using only Western terminology.
In addition to the exercises, information (and a discussion) is provided and discussion is facilitated on the topics of stress, stress management, and how to apply mindfulness to interpersonal communication and everyday situations. Each group session includes time for participants to reflect together on what they experience while practising mindfulness. Outside the sessions, participants are encouraged to practice each day for 30-45 minutes while listening to audiotapes and using the guided exercises (these include body-scanning, the mindfulness sitting exercise which focuses on breathing, as well as yoga stretching exercises). The group usually includes 10-30 members and is led by one or two trained instructors.
1.3 HOW THE INTERVENTION MIGHT WORK
The MBSR programme provides systematic training in mindfulness as a self-regulation strategy to reduce stress and manage emotion. The programme is intended to foster greater awareness of what happens in each moment through the application of an attitude of acceptance. MBSR is designed to help people avoid habitual negative thoughts, emotions and behavioural patterns. Instead, increased awareness and acceptance is seen as allowing for new ways to respond and cope both in relation to oneself and the wider world. Mindfulness training has been linked to changes in areas of the brain responsible for affect regulation, and to stress impulses reactions; in turn, these changes influence body functions such as breathing, heart rate and immune function (Davidson, 2003; Lazar, 2005; Hölzel, 2010).
1.4 WHY IT IS IMPORTANT TO DO THIS REVIEW
MBSR is increasingly widespread and it is important therefore to find out whether it is effective, for whom, and under what circumstances. Knowing such details can help to guide future research. A number of recent published reviews have suggested overall that MBSR may be effective in reducing the symptoms of anxiety, depression and stress. However, most such reviews have been narrative reviews rather than meta-analyses. This has led Hofmann et al. (Hofmann, 2010) to argue that “the field has become saturated with qualitative reviews” (p.170).
Quantified effect sizes in other meta-analyses we have identified were based on randomised controlled trials combined with quasi-experimental design studies (Baer, 2003; Carmody, 2009; Grossman, 2004; Ledesma, 2009; Hofmann, 2010). Baer found an overall Hedges' g-value of effect size of 0.59 for all outcomes, but this included both MBSR and Mindfulness Based Cognitive Therapy (MBCT) studies. Similarly, Carmody calculated an overall Hedges' g-value for effect size of 0.63 for psychological outcomes, but included control groups with both treatment-as-usual, waiting-list, and alternative treatments. Grossman reported an overall Cohen's d-value of effect size of 0.5 for studies of MBSR with combined outcomes of physical and mental well-being. Hofmann also included MBSR and other interventions like mindfulness based cognitive therapy in the same meta-analysis, reporting an overall Hedges' g-value of effect size for anxiety of 0.63 and 0.59 for mood symptoms. Bohlmeijer et al. (2010) included only controlled MBSR studies, and calculated an overall Hedges' g-value of effect size of 0.47 for anxiety outcomes and 0.32 for psychological distress outcomes. However the authors grouped together studies using waiting-list controls and studies where the control group was offered alternative active treatment.
A health technology assessment report from 2007 (searches conducted up to 2005) identified five broad categories of meditation practices of which mindfulness meditation was one (Ospina, 2007). In this instance, the meta-analysis was focussed on effects on hypertension, cardiovascular disease and substance abuse, and it did not specifically evaluate MBSR.
2 Objectives
To assess the effectiveness of MBSR in improving health, quality of life, and social functioning in adults.
3 Methods
3.1 CRITERIA FOR CONSIDERING STUDIES FOR THIS REVIEW
3.1.1 Types of studies
Studies of mind-body interventions such as MBSR are especially prone to bias introduced by the self-selection of study participants to intervention or control groups. For this reason, we have only included RCTs in this systematic review. We expected to find a sufficient number of such studies.
3.1.2 Types of participants
MBSR is a general method for self-regulation that has been applied to a variety of target groups: we therefore included all populations. There were two exceptions to this approach: both children (under the age of 18) and persons with cognitive impairment or severe mental illness were not included. This was because children are less able to be self-aware; MBSR is dependent on the ability of individuals to pay attention and to be able to remember from one moment to the next.
3.1.3 Types of interventions
We included studies of MBSR training programmes which had been based on the protocol elements specified by John Kabat-Zinn (Kabat-Zinn, 1990). This meant that to be considered, the intervention had to be explicitly termed ‘MBSR’ and contain all four of the requisite core elements, namely: body-scan exercises, mental exercises focusing attention on breathing, physical exercises focussing on the awareness of bodily sensations, and the practice of being fully aware during everyday activities. Studies of varying MBSR course duration and intensity were included. Studies that combined MBSR with other therapeutic approaches, such as cognitive therapy or art therapy, were excluded.
Waiting lists and treatment-as-usual were acceptable control groups. RCTs in which the control group had been offered alternative active treatment were also included, but these were analysed separately.
3.1.4 Types of outcomes
Primary outcomes were measures of mental health (anxiety, depression and stress/distress), somatic health (self-reported physical health inventories and somatic measures related to antibodies, heart rate or respiratory functions) and quality of life (only including measures designed specifically to measure quality of life, such as the WHO Quality Of Life Inventory). Secondary outcomes were social functioning (such as the ability to work, sickness rates, and self-reported measures of social functioning e.g., The Social Functioning Questionnaire SFQ) and measures of personal development (e.g., self-acceptance, empathy, coping and forgiveness). The different measurement scales and outcome groups are listed in additional Tables 4 and 5.
3.2 SEARCH METHODS FOR IDENTIFICATION OF STUDIES
3.2.1 Electronic searches
Electronic searches of bibliographic databases and open websites were conducted. We examined reference lists from the articles under consideration and asked key researchers within the field for information. In addition, we searched for ‘grey literature’ trials and for ongoing studies registered at www.clinicaltrials.gov. No publication, geographic, or language restrictions were applied.
3.2.2 Search terms
The following sources were searched at the outset of the project in July 2008 and again in September 2010: MEDLINE AMED (Allied and Complementary Medicine) PsycINFO EMBASE Ovid Nursing Full Text Plus British Nursing Index and Archive Cochrane Central Register of Controlled Trials (CENTRAL) SIGLE Web of Science® SveMed+ Dissertation Abstracts International ERIC Social Services Abstracts Sociological Abstracts International Bibliography of Social Sciences ProQuest
The Cochrane Collaboration’ search strategy includes a RCT search filter for identifying randomised trials in MEDLINE and this was used when searching this database. This filter was subsequently modified for other database searches. Appendix 15.1 contains full documentation of all the search terms used.
3.3 DATA COLLECTION AND ANALYSIS
3.3.1 Selection of studies
Two reviewers independently read the titles and available abstracts of the studies in order to exclude those that were obviously irrelevant. Any citation deemed potentially relevant by at least one reviewer was retrieved in full text form. Multiple papers reporting on the same study were linked together. Two reviewers (one with content expertise and the other with methodological expertise) independently read all the retrieved studies in order to determine whether they met the selection criteria (Appendix 12.1). The reviewers were not blinded to journal names, author names, author affiliations or the study results. Disagreements about the relevance of particular studies were resolved during discussions with a third reviewer with methodological expertise. Correspondence with investigators, where necessary, helped to clarify study eligibility. Those studies that met the screening criteria but did not meet all the inclusion criteria are listed in Section 11.2 (Characteristics of Excluded Studies), together with the reasons for their exclusion.
3.3.2 Data extraction and management
Information on study design and implementation, sample characteristics, intervention characteristics, and outcomes was extracted from studies. This information was entered on a paper form (see Appendix 15.3). The data extraction form included a coding list which was piloted on two of the selected studies at the outset of the data extraction phase. Two reviewers independently extracted data from all the studies. Disagreements were resolved through discussions with a third reviewer with relevant methodological expertise.
3.3.3 Assessment of risk of bias in included studies
Risk of bias was evaluated according to the criteria stated in the Cochrane Handbook (Higgins, 2008). Two independent reviewers assessed the issues of sequence generation, allocation concealment, the blinding of outcome assessors, the completeness of outcome data, outcome reporting, and any other potential sources of bias. Using the GRADE approach, further analysis of the quality of evidence was undertaken related to each of the key outcomes (Guyatt, 2008; Higgins, 2009). The quality of the body of evidence for each key outcome was rated as ‘High’, ‘Moderate’, ‘Low’, or ‘Very Low’.
3.3.4 Measures of treatment effect
As expected, only outcome data from (a number of) ordinal scales were found; no binary data were identified. We therefore calculated standardised mean differences (as Hedges' g-values) using the Comprehensive Meta Analysis program which is able to accept a variety of different data formats (Borenstein, 2009). Effect sizes were calculated for gain scores (post-minus pre-measurements in the control group were subtracted from post-minus pre-measurements in the treatment group). These results were then standardised using the post-test pooled standard deviation. In four studies the effect sizes were calculated from other data; in Astin (1997) from the F-values for the difference in change in the MBSR and control group; in Cohen-Katz (2005) and Creswell (2008) from the difference in mean change between the MBSR and control group and the corresponding p-values; and in Grossman (2010) from the difference in mean change between the intervention and control group and the corresponding F- values.
3.3.5 Unit of analysis issues
We assessed the unit of analysis of all the trials: one study was found to have randomised couples rather than individuals. The robust standard error analysis we used (see below) was able to process the data while accommodating for such dependencies.
3.3.6 Dealing with missing data and incomplete data
Study authors were contacted if missing information was needed (related, for example, to standard deviations). Most authors did not respond or were unable to retrieve the data. Some studies presented data visually and this made it possible to read data from the graphs (Anderson, 2007; Davidson, 2003; Plews-Ogan, 2005; Shapiro, 1998; Williams, 2001). In other instances we calculated standard deviations using standard errors, confidence intervals, t-values or p-values that related to the differences between the means in two groups (Anderson, 2007; Davidson, 2003; Lengacher, 2009; Moritz, 2006; Plews-Ogan, 2005; Williams, 2001). In only one instance was a study excluded from the analysis due to a lack of information (no SD or SE) (Alterman, 2004).
Means and standard deviations values were based on those stated in the original study publications, irrespective of how such missing data may have been processed in the primary analysis.
3.3.7 Assessment of heterogeneity
The degree of heterogeneity was evaluated both informally (by checking the overlap of the confidence intervals), and statistically (by estimating the total heterogeneity using tau2 values (where <0.05 indicates low heterogeneity). The percentage of the total variability due to heterogeneity was estimated using I2 values; 0% representing no heterogeneity, 50% indicating moderate heterogeneity and 75% indicating high heterogeneity (Higgins, 2003).
3.3.8 Assessment of publication bias
We investigated possible reporting biases using funnel plots and tested for funnel plot asymmetry using Egger's regression test (Egger, 1997).
3.4 DATA SYNTHESIS
All analyses were conducted with random effects models. When evaluating the outcomes for mental health, the results were first grouped separately into four constructs, namely: anxiety, depression, stress/distress and other measures of mental health (see Table 13.4). The majority of the studies identified included multiple measures of the same construct, and the sizes of effect were typically calculated for the same individuals. Since the covariance structure of these effect sizes was not reported in any of the studies, we used a newly developed robust statistical technique for estimating standard errors under such circumstances (Hedges, 2010).
This technique calculates standard errors using an empirical estimate of the variance: it does not require any assumptions regarding the distribution of the effect size estimates. Those assumptions that are required are minimal and generally met in practice. Simulation studies show that both confidence intervals and p-values generated this way typically reflect the correct size in samples, requiring as few as ten studies for the estimation of an average effect size, or between 20-40 studies for the estimation of a slope. This more robust technique is therefore beneficial because it allows all of the effect size estimates to be included in meta-analyses.
An important feature of this more robust standard error analysis is that the results are valid regardless of the weights used. For efficiency purposes, we calculated the weights using a method proposed by Hedges et al (Hedges, 2010). This method assumes a simple random-effects model in which study average effect sizes vary across studies (τ2) and the effect sizes within each study are equicorrelated (ρ). The method is approximately efficient, since it uses approximate inverse-variance weights: they are approximate given that ρ is, in fact, unknown and the correlation structure may be more complex. For the results we calculated, weights were used based on estimates of τ2 and I2, where ρ =0.80. Though not reported here, sensitivity tests were also conducted using a variety of ρ values; these indicated that the general results and estimates of the heterogeneity (τ2 and I2) were robust to the choice of ρ.
In addition to estimating an average effect for each of the four mental health constructs, we also calculated an average effect for mental health across all the studies and measures. Clinicians commonly view anxiety, depression and psychological stress/distress as different constructs. However, the actual questions used in the different inventories (many of which were often fairly similar) and the measurement of correlation (which were consistently high) cast doubt on whether the standard methods of measuring anxiety and depression do, in fact, always tap into different constructs in practice. The described analyses are therefore an explicit attempt to look at this difficult issue using both such approaches.
This robust standard error approach was also used to evaluate the outcomes of somatic health, quality-of-life measures, personal development and mindfulness, as well as for varying lengths of follow-up.
3.4.1 Subgroup analysis, moderator analysis and investigation of heterogeneity
Theoretical and empirical reasons suggest that, by and large, one may expect similar effects across chosen target groups, varieties of an intervention, and relevant outcomes. Nevertheless the following subgroup analysis was undertaken in order to explore potential differences in effects on mental health: Clinical and non-clinical samples (expecting a somewhat larger effect in studies of patients with established health problems compared to studies where participants were recruited from the general population) Psychological and somatic conditions (expecting a somewhat larger effect in studies of participants with psychological distress compared to studies of people with somatic problems) Effect of length of the MBSR intervention (expecting a somewhat smaller effect in studies that used a shorter MBSR programme compared to a standard approach) Effect of compliance (expecting a somewhat larger effect in studies where participants generally attended most of the programme versus studies where attendance was lower, and in studies where people spent more rather than less time practising at home) Effect of follow-up time (expecting effect sizes to diminish over time in studies with a longer follow-up period) Risk of bias (expecting a larger effect in studies with higher risk of bias). In this particular analysis we used the risk of bias scores as a scale Whether or not the authors claimed to have done an intention to treat (ITT) analysis (expecting somewhat lower effect estimates in studies that reported ITT analyses).
Each of these questions was investigated using a separate bivariate regression model. Each model was estimated using the robust standard error method outlined above (Hedges, 2010). Since this robust standard error method uses degrees of freedom based on the number of studies (rather than the total number of effect sizes), we elected to apply individual regression models instead of combined models. In Appendix 12.4 we provide a correlation matrix for the following variables: clinical (vs. non-clinical) samples, clinical somatic (vs. clinical psychological) samples, length of MBSR invention, attendance, follow-up time, risk of bias, and if the analysis was based on an intention-to-treat effect.
4 Results
4.1 RESULTS OF THE SEARCH
The original search in July 2008 identified 2,162 potentially relevant articles; a second search in September 2010 found 972 additional references. Based on our screening and inclusion criteria 31 studies were included in the review.
4.2 DESCRIPTION OF THE STUDIES
4.2.1 Included studies
The characteristics of the included studies are listed in Table 10.1 and 11.1. 20 studies recruited people with health problems: 13 of these included patients with somatic conditions (musculoskeletal disease, cancer, other chronic illness, HIV, cardiovascular disease and substance abuse (Bränström, 2010; Creswell, 2007; de Vibe, 2006; Grossman, 2010; Lengacher, 2009; Monrone, 2008; Plews-Ogan, 2008; Pradhan, 2007; Sephton, 2007; Speca, 2000; Speca, 2000; Surawy, 2005; Tacon, 2003). Seven studies included persons with psychological conditions (stress/distress, anxiety, mood disorder, aggression and stuttering) (Alterman, 2004; de Veer, 2009: Koszycki, 2007; Moritz, 2006; Nyclicek, 2008; Vieten, 2008; Willliams, 2001). 11 studies included people from the general population (Anderson, 2007; Carson, 2004; Cohen-Katz, 2005; Davidson, 2003; Klatt, 2009; Shapiro, 2005); five such studies used student samples (Astin,1997; Jain, 2007; Murrey, 2004; Oman, 2008; Shapiro, 2005). One study included prisoners (Murphy, 1995). Altogether 1,942 persons were randomised; 26 studies compared MBSR with waiting-list or treatment-as-usual controls.
Three of the studies included another intervention group in addition to the waitlist control group (Jain, 2007; Moritz, 2006; Plews-Ogan, 2005) and in these cases we used only the data from the comparison of MBSR with the waitlist controls. The results of four additional included studies were reported separately because they compared MBSR with other active interventions. Creswell (Creswell, 2008), for example, compared a standard eight-week MBSR course with a one-day MBSR course. Koszycki (Koszycki, 2007) compared MBSR with MBCT. Murphy (1994) compared MBSR with progressive relaxation training. And Oman (2008) compared MBSR with a generally similar mindfulness training called Easwaran's Eight-Point Program (EPP), and with treatment-as-usual. In this paper, only combined data from the groups receiving MBSR or EPP were reported.
In addition, we included — but could not use — data from one study (Alterman, 2004; see ‘Studies where data could not be used in the meta-analysis'). Two studies were reported in two publications: Sephton (Sephton, 2007) also presented results in Weissbecker (Weissbecker, 2002), and one study was presented both by Tacon (2002) and Robert-McComb (2004).
4.2.2 Excluded studies
188 studies were excluded either because they were neither primary studies nor RCTs, or because the intervention did not conform to the MBSR protocol. Reasons for exclusion are listed in Table 11.2.
4.2.3 Studies awaiting classification
Four studies are awaiting classification (Esmer, 2010; Schmidt, 2011; Vøllestad, 2011; Wong, 2011).
4.3 RISK OF BIAS IN INCLUDED STUDIES
4.3.1 Allocation concealment
The quality item with the lowest score was allocation concealment. Only nine studies reported adequate concealment of allocation. Most studies failed to state clearly how randomisation had been achieved.
4.3.2 Blinding
Blinding of participants and providers is impossible to achieve in studies where people receive stress reduction interventions. It is, however, possible to blind the assessors and this was done in ten studies.
4.3.3 Incomplete outcome data
Attrition was 15% overall and 25 studies reported all data, while only four studies had a definite incomplete reporting of all results. Nine studies reported intention to treat analyses data, and they used the last observation carried forward as the method for imputing missing data.
4.3.4 Selective reporting
Assessing publication bias, we detected no important funnel plot asymmetry (see Figure 13.13) and the Egger's r-test for funnel plot symmetry indicated an intercept value of 0.95 (95% CI -0.24, 2.15). When applied, a Fail-Safe N (Rosenthal,1979) analysis showed that the number of missing trials needed to raise the p-value to >0.05 was 689; a Fail- safe N (Orwin, 1983) analysis showed that the number of missing studies with zero effect — that would reduce the Hedges's g-value to <0.2 (indicating a small effect) — was 44.
4.3.5 Other sources of bias
Many studies are carried out by researchers believing in the intervention and who also provide the intervention and are responsible for the assessment. Other sources of bias were different assessors doing semi-structured interviews with the participants at baseline and after the intervention (Alterman, 2004), baseline differences between groups not accounted for (de Veer, 2009), some participants changed group after randomization (Oman, 2008), and some participants were given additional sessions with a therapist (Surawy, 2005).
4.4 EFFECTS OF THE INTERVENTIONS
4.4.1 MBSR vs. waiting-list/treatment-as-usual
All effect sizes are expressed using Hedges' g-values (Hedges 1985), and conventionally a value of 0.2-0.5 signifies a small effect, 0.5-0.8 a moderate effect and values >0.8 signifies a large effect of the intervention (Cohen, 1988). Positive values indicate beneficial effects.
Converting effect sizes to percentile values is a useful way to illustrate possible clinical importance: an effect size of 0.53, for example, indicates that the average person in the intervention group will be placed at the 30th score percentile for the control group.
Table 11.5 and Figures 13.4-13.7 show that the average effects were fairly similar for anxiety (0.53, 95% CI 0.43, 0.63), depression (0.54, 95% CI 0.35, 0.74), stress/distress (0.56, 95% CI 0.44, 0.67) and other measures of mental health (0.48, 95% CI 0.34, 0.61). Values for heterogeneity, from tau square analysis, were very small and ranged from 0 to 0.003. 26 studies with 79 different outcome variables (of anxiety, depression, stress/distress and various other measures of psychological functions) contributed to the meta-analysis of mental health in which the robust standard error approach was used (Figure 13.8). The overall effect size for the composite measure of ‘mental health’ was 0.53 (95% CI 0.46, 0.61). Again, heterogeneity across the studies was low: the values were tau2 = 0 and I2 = 0.
The effects on measures of personal development (0.50, 95% CI 0.35, 0.66), quality of life (0.57, 95% CI 0.17, 0.96), and mindfulness (0.70, 95% CI 0.05, 1.34) were also of moderate size (Figures 13.9-13.11). However, as shown in Figure 13.12, the effect size was somewhat smaller for measures of somatic health (0.31, 95% CI 0.10, 0.52). Results for quality of life and mindfulness were somewhat heterogeneous across trials with tau2 values of 0.07 and 0.40.
For mental health as a composite outcome, there was an insignificant difference in effect size between studies in which persons were recruited because of stress or diagnosed problems (in other words, from clinical populations) and target groups which had been recruited from the general population (p=0.19). Likewise, studies of people with somatic problems as entry criteria achieved a very similar effect on average to those studies in which people with psychological difficulties were recruited (p=0.96) (Table 11.6).
The effect size for ‘mental health’ rose slightly with increasing intervention length (between 6 and 28 hours), but again this increase was not statistically significant (p=0.16).
18 studies reported on course attendance which ranged from 65% to 92%. There was a significant increase in effect on mental health for each hourly increase in attendance (reported as averages per study) (p <0.01). Only 13 studies described self-reported time spent practising MBSR techniques at home (with an average range per study of between 7 and 45 minutes). In this analysis, length of self-reported time spent practicing MBSR techniques at home did not appear to increase mental health outcome scores (p=0.44).
For follow-up time, we first compared the effect at post-intervention in studies with data (9 studies) and without follow-up data (17 studies) and found no difference. We then assessed the effect of the number of months of follow-up on the reported effect size. There was a slight, but statistically significant, decrease in effect size on ‘mental health’ for each additional month of follow-up (p<0.05).
A slight decrease in effect size was seen as risk of bias increased, but this finding was not statistically significant (p=0.29). Neither were there significant differences in effect sizes between those studies reporting results as intention to treat (ITT) analyses and studies reporting per protocol data (p=0.13).
Mindfulness was measured in seven studies (measures used are listed in additional Tables 2 and 3): six reported increases at the post-intervention stage, while one study showed an increase only at four months follow-up (Pradhan, 2007). Two studies performed mediation analysis, suggesting that the effect on the outcomes were mediated by the increase in mindfulness scores (Bränström, 2010, Nycklicek, 2008). Because few studies measured mindfulness and because we do not have access to data on individuals in the studies, further mindfulness mediator/moderator analyses could not be performed.
Unfortunately, very few studies measured social functioning. One study reported on ability to work, but the numbers of people involved were too small to allow conclusions to be drawn. There were no reports on adverse events or costs in any of the studies.
4.4.2 MBSR vs. Alternative active interventions
The data from these studies are treated separately and the effect sizes are not pooled.
Koszycki et al. (2007) compared an eight-week (27.5 hour) MBSR course with a 12-week (30 hours) cognitive behavioural therapy course for 53 patients with moderately severe social anxiety disorder. All sessions were videotaped and reviewed to assess protocol fidelity. Homework forms were reviewed each week. Both interventions produced meaningful clinical changes. The MBSR group showed high to moderate beneficial effect judged by within group Hedges' g-value effect sizes on measures of social anxiety (1.42, CIs not given), mood (0.66), disability (0.63), and quality of life (0.53). Patients in the cognitive therapy group improved significantly more than those in the MBSR group in terms of social anxiety. There were no between-group differences in the other outcomes. The MBSR programme had a dropout rate of only 15%.
Oman et al. (2008) compared an eight-week (12 hour) MBSR course with an alternative eight week (12 hour) programme (on Easwaran 8-point mindfulness), while the third group was a wait-list control group of 44 college students. Because the unreported data results were similar for both the MBSR and EPP participants, both groups were analysed together and compared to the wait-list control group. The between-group Hedges' g-values for effect sizes for the main outcomes at post-intervention (and at the eight weeks follow-up) were 0.44 (0.50) for perceived stress, 0.33 (0.44) for rumination, and 0.33 (0.30) for forgiveness (confidence intervals not given). There were no significant changes in measures of hope.
Murphy (1994) compared the effect of a six-session (12 hour) MBSR course with six two-hour sessions of progressive muscle relaxation (PMR) for 31 inmates who had alcohol abuse and aggression problems. No substantial differences were found on measures of anger (using the State Trait Anger Expression Inventory), egocentricity (using Self Focus Sentence Completion), and stress reactivity measured by the post-stress testing of salivary cortisol at the post-intervention stage.
Creswell et al. (2008) compared an eight week (24 hour) MBSR course with a one day (6 hour) MBSR course among 48 HIV+ people experiencing distress and scores of >4 on the Patient Health Questionnaire-9 scale). CD4+ T lymphocyte counts were shown to decrease in the one-day control group, but not among participants in the full MBSR course. The between-group Hedges' g-value of effect size was 0.74 (CI not given).
4.4.3 Studies where data could not be used in the meta-analysis
Alterman et al. (2004) compared the effect of an eight-week (23 hour) MBSR course with treatment-as-usual for 31 substance-abuse recovery inpatients at post-intervention and at five months follow-up (Alterman, 2004). The data were analysed using repeated measures analysis of variance at three time points. The intervention group improved more than the control group in terms of self-reported medical problems when analysed as a group over three follow-up times (p=0.007). However, because only mean values were reported, a Hedges' g-value of effect size could not be calculated. No significant group differences were found for measures of psychological health.
5 Discussion
5.1 SUMMARY OF THE MAIN RESULTS
It is encouraging to see that the MBSR mind-body intervention has been analysed in substantial numbers of randomised controlled trials. This review has reported on more trials than ever before: 31 RCTs were selected, with a combined total of 1,942 participants. The overall effect size for the combined outcome of mental health was moderately large (Hedges' g-values = 0.53, 95% CI 0.46, 0.61). The effect sizes were remarkably similar across a range of target groups (with mild to moderate distress), intervention forms, outcome measures and settings. Heterogeneity was therefore low.
Many of the studies we included provided several different measures of the same construct and outcome measurements that were obviously interdependent. Failure to account for such dependencies — in other words, calculating an average ‘anxiety effect’ based on measurements with different anxiety scales — necessarily results in erroneous standard errors and will compromise any inferential statistics generated. Deciding on a criterion for electing only one outcome measure to include in the meta-analysis can be equally problematic. Statistical dependencies were also evident in follow-up measures post-test. As far as we know, this study is amongst the first to utilise a new method for estimating robust standard errors under such circumstances. This method makes it possible to use more information in the data-set than has traditionally been the case (Hedges, 2010).
5.2 OVERALL COMPLETENESS AND APPLICABILITY OF EVIDENCE
A number of MBSR evaluations have been published in this specialist knowledge field in the last decade. Baer identified four randomised trials in 2003 (Baer, 2003) and all of these are included in our study. Grossman (Grossman, 2004) reported on seven RCTs in 2004: one of these we classified as not being a randomised trial (Perkins, 1998). Carmody (2009) found 11 controlled studies: nine were classified by us as RCTs.
Later reviews have focussed on specific target groups. Ledesma & Kumano, for example, identified four trials on cancer patients (Ledesma, 2009). We have excluded three of these from our analyses — two because they included elements other than those stipulated in the traditional MBSR protocol (Herbert, 2001; Monti, 2005), and one because it took the form of a quasi-experimental study (Shapiro 2003). Hofmann identified seven randomised trials measuring anxiety or depression (Hofmann, 2010) and all of these are included in our study. Bohlmeijer identified eight RCTs studying patients with a chronic medical condition (Bohlmeijer, 2010). Seven of these are included in this work, while one was excluded because it deviated from the standard MBSR protocol (Monti, 2005). Chiesa (Chiesa, 2009) included seven trial studies of healthy people, and all of these are included in our study.
Of the 26 studies used in our meta-analysis, five included persons with various psychological problems; 11 of the studies targeted people with various somatic conditions; and ten recruited people from the general population. The intervention effect has thus been evaluated across a broad spectrum of target groups. Study settings in a number of different countries (Norway, Sweden, Germany, Switzerland, Holland and the USA) contributed to the analysis, further serving to increase the applicability of the evidence.
Studies that implemented major modifications to the standard MBSR protocol were not included. However, studies of varying intervention length were accepted if the researchers had adhered to the MBSR principles as stated by Kabat-Zinn (Kabat-Zinn, 1990). Relatively few studies included follow-up data, and none included long-term follow-up data: the evidence therefore for the long-term effects of the intervention is clearly limited. All control groups received no treatment or treatment-as-usual. Control conditions therefore varied and it was often difficult to determine what the alternative conditions had been.
Unfortunately, only two trials provided data on social functioning (Nyklicek, 2008; de Vibe, 2006) and the ability to work (de Vibe, 2006) and there was a paucity of data related to functional outcomes. No explicit reporting on possible adverse effects or costs was provided. Such information should be addressed in future trials.
5.3 QUALITY OF THE EVIDENCE
The quality of the studies varied and the overall risk of bias was high for several studies (Davidson, 2003; Cohen-Katz 2005; Alterman, 2004; Astin, 1997; Lengacher, 2009; Murray 2004; Plews-Ogan, 2005; Shapiro, 2005; Weissbecker, 2002). However, it was encouraging that high-quality trials were also found (Bränstöm, 2010; Grossman, 2010; Jain, 2007; Moritz, 2006; Morone, 2008; Nyklicek, 2008; Pradhan, 2007; Speca, 2000). Effect sizes did not, however, differ significantly between studies carrying different risk of bias (p = 0.32, see additional tables 4). Judgements about evidence and recommendations in healthcare are complex. The GRADE system has been developed to improve judgements about the quality of evidence (GRADE, 2008). Grading of the evidence showed that the quality is high for evidence of effect on the composite score of mental health as well as for measurements of stress/distress, but low for measurements of effect on quality of life, and moderate for effects on other outcomes (Figure 13.14).
5.4 POTENTIAL BIASES IN THE REVIEW PROCESS
All steps in the analyses were undertaken by researchers with content and methodological expertise.
Estimation of effects using the more robust method of variance estimation we applied showed typically similar effect size estimates compared to estimates made using the conventional method. The confidence intervals, however, were narrower. It was notable that we were able to make use of most of the data provided in the studies. We also avoided the often haphazard choice of which outcome to include in a meta-analysis in those instances where several measures of the same construct were presented in the primary studies. We anticipate that this new statistical method will become a standard technique in future meta-analysis.
5.5 AGREEMENTS AND DISAGREEMENTS WITH OTHER STUDIES OR REVIEWS
Overall, the effect sizes we estimated are relatively similar to the findings presented in other review evaluations of MBSR. This holds true for measures of anxiety, depression, stress, somatic health, and quality of life. This was not the case, however, with regard to Toneatto's study in which MBSR was shown to have no effect on depression and anxiety (Toneatto, 2007). Toneatto's finding though, we would contend, was due to comparisons of MBSR being made with alternative interventions in studies with varying designs. We suggest that the effect size compares favourably with a recent meta-analysis of psychological treatments of depressive symptoms in patients with medical disorders (van Straten, 2010). After removing two outliers, the data showed an overall effect size of d=0.42 (95% CI 0.27, 0.58) for the 15 controlled studies comparing psychological treatments with a waitlist or care-as-usual control group. Likewise, the effect size is in the same range as those recently reported for interpersonal psychotherapy for depression (Cuijpers, 2011). The potential for MBSR as a useful intervention for improving mental health, we argue, is therefore promising.
Based on the assumption that many self-reported mental health outcomes are actually rooted in similar aspects of mental functions, we developed a single composite measure of mental health based on the outcomes for anxiety, depression, stress/distress and other mental health outcomes. These latter outcomes included measures of emotional disturbance and regulation, anger, worry, rumination, relaxation, and life orientation. This mental health measure captured data from all 26 studies; the measure included 79 of the 132 outcomes. Three other reviews (that also included non-randomised studies) measured ‘mental health’ as a single construct and the results were in the same range as our own (Baer, 2003; Grossman, 2004; Carmody, 2009).
5.5.1 Subgroup analyses
All subgroup analyses were conducted using the single composite mental health outcome measure as the dependent variable. The correlation matrix of the variables is shown in additional Table 11.6. A somewhat larger effect size among patient populations (16 studies) than non-clinical populations (ten studies) was expected. We hypothesised that effects would be larger in clinical populations with psychological problems (five studies) than in somatic clinical populations (11 studies). However, neither of the comparisons showed any significant difference, and both Grossman (2004) and Carmody (Carmody, 2009) reported similar findings. A possible explanation for this is that all the studies included participants who were self-selected. Given that the MBSR intervention is a well-known intervention for stress-related problems, those included in the studies might therefore be expected to be more similar in terms of their level of mental health problems than the different group categories might suggest. Another explanation for the similarity of effects across the different groups in terms of distress is because the studies on somatic health problems mainly included patients with chronic musculoskeletal problems, and the studies on psychological problems included only patients with minor mental problems.
However, there is evidence to suggest that the effect is larger for people who have substantially higher levels of mental health problems. One study which included patients with clinical psychiatric diagnoses (Koszycki, 2007) found a larger effect size, as did Grossman (2010) and de Vibe (2006), for subgroups of patients with higher levels of psychological symptoms. More studies should therefore attempt to elucidate which groups would benefit most from MBSR interventions and whether or not there is a floor effect (i.e., a particular level of symptoms that would be needed to demonstrate an effect).
Among the nine studies with follow-up data at 1-6 months, the effect size was shown to decrease slightly over time. More studies with longer follow-up periods are thus needed. Most trials offered the intervention to the control group immediately after the end of the intervention period. While this may be understandable from a practical or perhaps an ethical point of view, doing this destroys the possibility of examining evidence on long-term effects. One study (Pradhan, 2007), for example, gave three refresher classes in the four months follow-up period. A significant increase in the effects on psychological distress, well-being and mindfulness at follow-up was found when compared to post-intervention. We recommend further investigation to identify what will be required to maintain such treatment effects over time.
We expected the lengths of the intervention, attendance and home practice to influence the effect size to some degree, but only found this to be true for attendance. The length required for MBSR course interventions to have an effect is thus still unknown. It should also be noted that the effect may occur due to moments of insight which lead to a change in the way people view themselves and the world. This may be due as much to a person's readiness to change as from the length of an MBSR course. In a more detailed analysis of dose-response, Carmody (2009) did not find any significant effect from the length of an MBSR course or assigned home practice. But we do not know, however, anything about the quality of the actual practice undertaken. One could argue therefore that a 30-minute daily practice routine which lacks attention or focus may actually be less effective than learning instead to be mindful in everyday life — this would be very difficult to measure and evaluate.
Furthermore, different types of practice may have different effects on different outcomes, as shown in a pre-post study of 174 participants assigned to different types of MBSR classes (Carmody, 2008). When analysed on the basis of more careful recording, Rosenzweig (2010) showed that the effect varied both as a function of clinical condition and compliance. A recent uncontrolled study showed that home practice predicted not only reductions in self-reported stress, but also changes in brain grey matter density in the right amygdala, an area involved in stress reactions (Hölzel, 2010).
Attendance was found to be associated positively with the effect of the MBSR intervention in seven of the 11 studies examining this possible predictor. Attendance may be a measure of motivation or an indicator that participants found the intervention useful. It may simply be that seeing a course through to the end is necessary for a course to have effect. We suggest that this issue should be investigated further. This could be achieved by, for instance, trying to measure motivation, interviewing those who complete the courses as well as any dropouts, and measuring the effect of MBSR several times during the course period in order to explore whether attendance mediates the effects.
Eight studies reported intention to treat (ITT) data, and showed a slightly smaller mental health effect size (0.47) relative to the 18 studies with non-ITT data (0.59). The difference, however, was not significant. On the whole, attrition was low (ca. 15%). The data suggested no significant differences in average mental health effect size due to variations in risk of bias. However, it was somewhat difficult to distinguish between inadequate reporting and a de facto high risk of bias.
6 Authors' conclusions
6.1 IMPLICATIONS FOR PRACTICE
There is moderate- to high-quality evidence of a consistent and moderately large effect of Mindfulness Based Stress Reduction (MBSR) on health and quality of life. The intervention appears to improve measures of personal development, including empathy, coping, and a sense of coherence, as well as enhancing mindfulness.
Consistent effects across different populations, intervention forms and comparisons further enhance the relevance of the intervention. While MBSR clearly alleviated symptoms of stress and distress (and mental health more broadly defined), it also had effects on measures of personal development and quality of life. MBSR might be an attractive option for those interested in improving the way they cope with stress.
MBSR is group-based and can be delivered by non-medical personnel who have been given sufficient training and have experience in teaching and practising mindfulness.
6.2 IMPLICATIONS FOR RESEARCH
Further studies should explore ways to enhance the effects of MBSR interventions. To achieve this, qualitative design studies may prove to be valuable in gaining insight into participant perception and help to identify ways to involve participants more, thus strengthening the effects. However, when evaluating actual effects, RCTs must remain the preferred design; further uncontrolled studies are not needed. Longer follow-up periods are also required in order to assess and address long-term effects. Better reporting of randomised controlled trials is also urgently needed and future research should include head-to-head comparisons with other interventions. Well-designed primary studies ought to explore the effects of the length of the intervention as well as reported home practice. As this field rapidly evolves, we anticipate further combinations of both applied and basic approaches. Investigations of changes in brain and body functions may, for example, be embedded within trials. Such designs could potentially shed new light on mechanisms and interventions for change. New trials should include measures of mindfulness, preferably using the Five Facet Mindfulness Questionnaire (Baer, 2006). All trialists should attempt to share data, as many topics related to mechanisms may be explored in individual patient data meta-analyses.
7 Acknowledgements
The review draft was improved thanks to content and methods peer-reviewers, our English language consultant Simon Goudie, and the librarians Sølvi Biedilæ and Brynhildur Axelsdottir.
8 Differences between the protocol and the review
The use of the robust standard error approach in the analysis was not described in the protocol. This was because the method was published after the protocol had been accepted.
The suggested sensitivity analysis was processed using subgroup analysis (which relates to risks of bias and the application of ITT-analysis). We did not impute any missing information as attrition rates were low, and because neither risk of bias scores nor whether ITT-analysis was done, influenced the results.
Compliance was suggested both as a moderator and as part of the set of subgroup analyses. We chose the latter route.
Only seven studies measured mindfulness (in two different ways) and we chose not to perform the suggested moderator analysis.
With hindsight we should probably have avoided the mixture of concepts ‘subgroup analysis', ‘moderator analysis', and ‘sensitivity analysis'. We had some real subgroups (e.g. clinical vs. non-clinical target groups), some study level variables (e.g. risk of bias) and variables on the individual level (e.g. compliance and self-reported practice). While it seemed meaningful to investigate heterogeneity in effects by means of subgroup analysis for the first two groups (as described in the main text), in our judgement the latter variables can be treated as moderators in a meaningful way only if access to individual patient data is possible.
9 Sources of support
This study is supported by The Norwegian Medical Association, The Norwegian Knowledge Centre for the Health Services, Centre for Child and Adolescent Mental Health, Eastern and Southern Norway, and SFI Campbell at The Danish National Centre for Social Research.