PROTOCOL: Mindfulness Based Stress Reduction (MBSR) for improving health and social functioning in adults

Types of studies

Randomized controlled trials (RCTs), if carried out well, provide the most unbiased estimate of effect of all comparative designs. Studies of meditative techniques for psychosocial conditions are especially prone to bias introduced by any form for self-selection to intervention or control. Moreover, there is likely to be a sufficient number of RCTs of adequate size to include in meta-analyses. Hence, we will only include RCTs.

Types of participants

MBSR has been tried out on a variety of target groups. Since MBSR is a general method for self-regulation based on the ability to be attentive and aware that is common to most people, the review will include all populations (> 18 years of age) that have received the intervention.

Types of interventions

We will include studies on MBSR training programmes based on the elements set out in the protocol by John Kabat-Zinn (Kabat-Zinn 1990). To be included the intervention must contain all four core elements of MBSR: 1) body-scan exercises, 2) mental exercises focusing one's attention on the breath, 3) physical exercises with focus on being aware of bodily sensations, and 4) practicing being fully aware during everyday activities. As long as these elements are taught we will include studies with varying duration and intensity of the MBSR course. We will exclude studies that combine MBSR with other therapeutic approaches, such as cognitive therapy.

Acceptable control groups are no intervention, waiting lists, other interventions, combinations of other interventions and services as usual. We will include comparisons of different variations of MBSR; e.g. a short versus a long course.

Types of outcome measures

Primary outcomes are health as measured by reduction in stress, psychological distress, stress-related somatic health problems, and wellbeing as measured by improvement in quality of life and psychological wellbeing. Secondary outcomes are improvements in social functioning such as work ability and personal development (e.g. self-acceptance, empathy, coping and relationship satisfaction). Moderator variables are compliance (measured through number of sessions attended and the degree to which participants actually practice), and increased mindfulness. Only studies that report measurements on outcomes from standardised scales, e.g. Becks Depression Inventory - BDI, will be included. We will check whether original or adapted versions of the different scales were used.

Primary outcomes

There are a variety of ways to measure the primary outcomes. There is often a strong correlation between measures of health, illness and wellbeing, and many inventories can be understood to measure the same underlying process (Koivumaa-Honkanen 2004). A detailed listing of which scales and subscales used in various studies considered for meta-analysis is necessary together with a critical view on how they are labelled (a measure of quality of life may be labelled a measure of health in another study). Care will be taken to meta-analyse only measurements on scales that have been shown to measure the same underlying phenomenon. Commonly used measures are symptom checklists reporting either global measures or subscales. Examples of these are SCL90, SCL25, SCL5, SF36 and SF12. Some of these are used as a measure of health-related quality of life (e.g. SF36) while others have been used as a measure of psychological distress (e.g. SCL5). Many scales that measure specific aspects of psychological distress are also used, like anxiety (Spielberger State and Trait Anxiety - STAI), depression (Becks Depression Inventory - BDI) and burnout (Maslach Burnout Inventory - MBI). In addition there are scales measuring other aspects of psychological distress such as worry, rumination, fear, anger, hope and mood. A positive aspect of quality of life is measured by scales of psychological wellbeing, that often include a cognitive evaluation of satisfaction with life in addition to evaluating the degree of positive feelings of happiness and the absence of unhappy feelings.

Secondary outcomes

Social function. We are interested in seeing whether there are studies reporting on the effect of MBSR on social functions like work ability or activities of daily living, although we do not expect to find many studies that measure this.

Moderator variables

Compliance is measured by the length (number of hours of the MBSR course, the attendance at the MBSR course and the degree of reported mindfulness exercise. This will allow us to see if it is possible to establish a dose-response relationship between the intervention and the outcomes.

Lists of outcome measures which are included or excluded will be published.

Outcomes will typically be measured post-intervention, and at 3 or 6 month, at 12 month follow-up and longer if there is sufficient data. We will also document service cost if data on this is included in the primary studies. Included studies must contain sufficient information to make possible the calculation of the relative risk and/or standardized mean difference for primary outcome variables.

Electronic searches

MEDLINE

AMED (Allied and Complementary Medicine)

PsycINFO

EMBASE

Ovid Nursing Full Text Plus

British Nursing Index and Archive

Cochrane Library, 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

Searching other resources

We will also search for ongoing studies in ClinicalTrials.gov. Furthermore, we will make contact with MBSR developers, practitioners and independent researchers to identify unpublished reports, ongoing studies and studies that did not come up in our search.

Selection of studies

Two reviewers will independently read the titles and available abstracts to exclude obviously irrelevant reports. Any citation deemed potentially relevant by at least one reviewer will be retrieved in full text. Multiple reports of the same study will be linked together. Two reviewers (one content expert and one with methodological competence) will independently read all retrieved studies to determine whether they meet our selection criteria (described above and in Appendix 1). Readers will not be blinded as to journal name, author names, author affiliation or results. Disagreements will be resolved by consensus with a third author with methodological expertise. We will list potentially relevant, but excluded studies with an explanation as to why they were not included.

We will correspond with investigators, where necessary, to clarify study eligibility.

Data extraction and management

Information on study design and implementation, sample characteristics, intervention characteristics, and outcomes will be extracted from studies and entered into a paper form, see Appendix 2. If important information is missing, we will contact authors of the particular study to obtain the data. A coding list is incorporated in the data extraction form and will be piloted on two papers at the outset of the data collection phase (may result in minor adjustments). Two reviewers will independently extract data from all studies, one is a content specialist and the other has methodological expertise. If differences between raters occur, these will be discussed in order to refine coding schemes. Persisting disagreements that cannot be resolved by discussing with a third reviewer will be addressed by contacting the study authors. If this is unsuccessful, the disagreement will be recorded in the review. Multiple reports from the same study will be coded separately before combining information across reports.

Assessment of risk of bias in included studies

The risk of bias will be described in the “Risk of bias” table included in RevMan and the risk will be judged according to criteria set out in chapter 8 in the Cochrane Handbook (Higgins 2008). We will describe and judge sequence generation, allocation concealment, performance bias, blinding of assessors, incomplete outcome data, selective outcome reporting and other sources of bias like trial ended early. The nature of the intervention makes blinding of the participants and the course instructors impossible, but outcome assessors and those involved in the randomization process can be blinded. With regard to incomplete outcome data, we will assess dropout rates and the use of intention to treat (ITT) analysis.

Measures of treatment effect

We expect to encounter continuous data, typically in the form of measurements on a scale. We will extract data on final value scores. When available we will include in the analysis estimates of the treatment effect adjusted by taking into account baseline measurements. If standard deviations are not reported we will attempt to calculate them from standard errors, confidence intervals, t-values or p-values that relate to the differences between means in two groups. A few outcomes may be dichotomous and we will extract numbers for these outcomes (sample size will also have been collected). We will calculate effect measures using odds ratios for dichotomous data and standardized mean differences for continuous data.

If studies report multiple measures of the same construct at different points in time, we will conduct separate meta-analyses for outcomes measured at different points in time.

Unit of analysis issues

We will assess the unit of analysis of all the trials and determine whether individuals were randomized in groups or individually. We do not expect to find cluster-randomised trials. If we do, we will check for unit-of-analysis errors. For trials that use randomization by groups, results will be presented with proper control for clustering as set out in the Cochrane Handbook. To do this we need information about intra-class correlation coefficient (ICC). To determine the ICC we will use estimates in the primary trials on a study-by-study basis. If such information is not available we will use external estimates as described in the Cochrane Handbook.

Dealing with missing data

In the event of missing data, we will contact research authors in order to try to retrieve missing information due to incomplete reporting. We will address the potential impact of the missing data on the findings of the review in the assessment of risk of bias and in the discussion section. In the case of missing information on standard deviations for continuous outcomes we will impute data in order to include these studies in a sensitivity analysis.

Assessment of heterogeneity

We will measure heterogeneity both informally (checking overlap of confidence intervals) and statistically by the chi-square test and the I-squared statistics (Higgins 2002). Care will be taken in the interpretation of the chi-squared test, because of its low power. Expecting some heterogeneity that cannot readily be explained, we will use a random-effects meta-analysis model.

Assessment of reporting biases

We will investigate possible reporting biases by means of funnel plots and testing for funnel plot asymmetry using Egger's test. If we find important asymmetries, possibly due to small-study effects (the tendency for effect sizes from small studies to deviate from effect sizes from large studies), we will undertake a sensitivity analysis using the “trim and fill” method to correct for the asymmetry (Egger 1997).

Data synthesis

For mental health we will group results from measurement scales separately for anxiety, depression and stress/distress. If a study offers multiple measures of the same construct we will average the effect sizes from these outcomes. In a second level of analyses we will integrate all standardized effect sizes for mental health within single studies by calculating the mean. We will then synthesize these effect sizes for “mental health” across studies. It is a common view among clinicians that anxiety, depression and psychological distress are different constructs. However, studying the questions in inventories (which are overlapping), and measuring correlation (which is always high), one becomes doubtful of whether it holds true that the usual way of measuring e.g. anxiety and depression really taps into different constructs. The described two meta-analyses is an explicit attempt to look at this difficult issue both ways. As for physical health and social functioning, most measures will clearly represent separate constructs (e.g. blood pressure and pain). If the sample size varies between scales measured in a single study (that measures the same construct), we will weigh them for sample size when calculating the average score.

Inverse variance methods will be used to pool SMDs across studies, so that each effect size is weighted by the inverse of its variance in an overall estimate of effect size. Confidence intervals of 95% will be used for individual study data and pooled estimates. Binary outcomes will be analysed by calculating odds ratios with 95% confidence intervals.

We expect that all trials include measurements at the end of treatment. We also hope for medium-term follow-up (typically at three to six months), and possibly longer (if data are available).

Subgroup analysis and investigation of heterogeneity

We will perform the following subgroup analysis to explore possible differences in outcome effects:

Clinical and non-clinical populations (expecting a larger effect among patients with established health problems).

Sensitivity analysis

We intend to perform the following sensitivity analysis:

Removing the studies with large risk of bias to see whether an analysis of the studies with low risk of bias gives a different result.