Criteria for considering studies for this review
Types of studies
All randomised controlled trials (RCTs) assessing the effects of yoga in women with breast cancer undergoing treatment or who have completed treatment, or both. Both full text and abstract publications will be eligible if sufficient information is available on study design, characteristics of participants, interventions, and outcomes.
Types of participants
Women with a histologically confirmed diagnosis of non-metastatic or metastatic breast carcinoma (Stage I - IV) as defined by the American Joint Committee on Cancer (AJCC) tumor-node-metastasis (TNM) system (Compton 2012).
Women diagnosed with breast cancer and who have completed treatment (that is, completed initial management of Stage I - IV breast cancer) will also be eligible.
No limits will be applied regarding age groups or settings.
Studies including participants with other cancer types will be excluded unless the outcomes for the breast cancer subgroup are reported separately.
Types of interventions
Any form of yoga will be eligible as the experimental intervention (for example Hatha yoga, Ashtanga yoga, Iyengar yoga, Integrated yoga therapy, Viniyoga, Bikram Yoga, Sivananda yoga, Kundalini yoga, Tibetan yoga, Yoga of Awareness, or any other yoga form). Studies that do not mention a specific form of yoga but simply describe their intervention as 'yoga' will also be eligible. Interventions should include at least one of the following: yoga postures, breath control, meditation, and lifestyle advice (based on yoga theory or traditional yoga practices).
Studies on multimodal interventions such as mindfulness-based stress reduction, mindfulness-based cognitive therapy, or the Mind Body Program for Cancer by the Benson-Henry Institute for Mind Body Medicine (that includes yoga amongst other therapies) will be excluded as the relative effects of yogic practices cannot be assessed separately in such programs.
Attention control, waiting list control, treatment as usual, no therapy, or any other active therapy will be eligible as the comparator.
Breast cancer treatments such as chemotherapy, radiotherapy, or anti-hormonal therapy, and supportive care will be allowed as long as the co-interventions are intended to be comparable between groups.
Types of outcome measures
Health-related quality of life, assessed by any validated generic or disease-specific self-report scale
Depression, assessed by any validated self-report or clinician-rated scale
Anxiety, assessed by any validated self-report or clinician-rated scale
Fatigue, assessed by any validated self-report scale
Sleep disturbances, assessed by any validated self-report scale
When there is more than one measure for an outcome, standard instruments will be preferred over novel instruments and multi-item instruments over single-item instruments.
Search methods for identification of studies
We will search the following databases.
(a) Cochrane Breast Cancer Group (CBCG) Specialised Register. Details of search strategies used by the CBCG for the identification of studies and the procedures used to code references are outlined in the CBCG's module at www.mrw.interscience.wiley.com/cochrane/clabout/articles/BREASTCA/frame.html. Trials with the key words "breast cancer", "early breast cancer", "locally advanced breast cancer", "advanced breast cancer", "high risk", "yoga", and "alternative/complementary therapy" will be extracted and considered for inclusion in the review.
(b) MEDLINE (via PubMed). See Appendix 1.
(c) EMBASE (via EMBASE.com). See Appendix 2.
(d) World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) search portal (http://apps.who.int/trialsearch/Default.aspx) for all prospectively registered and ongoing trials. See Appendix 3.
(e) Clinicaltrials.gov (http://clinicaltrials.gov/). See Appendix 4.
(f) IndMED (http://indmed.nic.in/indmed.html). See Appendix 5.
(g) CENTRAL (2013, Issue 3). See Appendix 6.
Searching other resources
(a) Bibliographic searching.
We will try to identify further studies from reference lists of identified relevant trials or reviews. A copy of the full article will be obtained for each reference reporting a potentially eligible trial. Where this is not possible, attempts will be made to contact authors for them to provide additional information.
(b) Grey literature searching.
Conference proceedings of the following congresses and annual meetings of societies will be searched for relevant abstracts:
International Congress on Complementary Medicine Research (ICCMR);
European Congress for Integrative Medicine (ECIM);
American Society of Clinical Oncology (ASCO).
Data collection and analysis
Selection of studies
Titles and abstracts of studies identified during the literature search will be screened independently by two review authors (HC and RL). Potentially eligible articles will be read in full by two review authors (HC and RL) to determine whether or not they meet the eligibility criteria. Disagreements will be discussed with a third review author (PK) until consensus is reached. If necessary, additional information will be obtained from the study authors.
Excluded studies will be recorded in the 'Characteristics of excluded studies' table.
The study selection process will be documented in a PRISMA flow chart (Moher 2009).
No language restrictions will be applied. Studies in languages other than English, German, French, Russian, Chinese, Norwegian, Swedish, or Islandic will be professionally translated.
Data extraction and management
Two review authors (PK and SL) will independently extract and enter data from all included studies into the 'Characteristics of included studies' table in the Review Manager software (RevMan). Disagreements will be discussed with a third review author (HC) until consensus is reached. A third review author (HC) will check the extracted data.
The information collected will include the following.
Methods: study design, methods of allocation, allocation concealment, blinding, dropout rates and reasons for dropping out.
Participants: country of origin, setting, sample size, diagnosis, age, ethnicity.
Intervention: type, program length, frequency, duration (for experimental and comparator interventions).
Outcomes: type of outcomes, assessment instruments, assessment time point, and follow-up time point.
For studies with more than one publication, the first publication will be considered as the primary reference but data will be extracted from all of the publications.
Assessment of risk of bias in included studies
Two review authors (PK and SL) will independently assess risk of bias using Cochrane's risk of bias assessment tool (Higgins 2011). Risk of bias will be assessed for the following domains.
Random sequence generation.
Blinding of participants and personnel.
Blinding of outcome assessment.
Incomplete outcome data.
Selective outcome reporting.
Other sources of bias.
Each domain will be judged as either:
'low risk of bias' if the requirements are adequately fulfilled, as described in Higgins 2011;
'high risk of bias' if the requirements are not adequately fulfilled, as described in Higgins 2011;
'unclear risk of bias' if insufficient data for a judgement are provided.
Risk of bias will be incorporated in judging the quality of evidence for each outcome according to the GRADE recommendations (Guyatt 2008).
Measures of treatment effect
Primary outcomes will be classified as continuous outcomes and expressed as standardised mean differences (SMD) with 95% confidence intervals (CI) according to the Cochrane Handbook for Systematic Reviews of Interventions, chapter 7, section 7.7.3 (Higgins 2011). SMD will be calculated as the difference in means between groups divided by the pooled standard deviation using Hedges' correction. Where available, final values will be preferred over change scores. A positive SMD will be defined to indicate beneficial effects of the experimental intervention compared to the comparator intervention for quality of life, while a negative SMD will be defined to indicate beneficial effects for mental health and cancer-related symptoms. If necessary, scores will be inverted by subtracting the mean from zero (Higgins 2011).
Secondary outcomes will be classified as dichotomous outcomes and expressed as risk ratios (RR) with 95% CI. RR will be calculated by dividing the risk of an event in the experimental group (that is the number of participants with the respective outcome divided by the total number of participants) by the risk of the event in the control group. RRs less than 1.0 will be defined to favour the experimental group (that is fewer adverse events than in the comparator group) and RRs greater than 1.0 will be defined to favour the comparator group (Higgins 2011).
Unit of analysis issues
Special issues in the analysis of studies with non-standard designs will be handled according to the suggestions of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). For cross-over trials, paired data will be analysed if available. Elsewise, only data from the first active treatment phase will be used. If repeated outcome assessments are presented, the time frames will be defined as short term (up to six months), medium term (six to 12 months), and long term follow-up (more than 12 months). For studies that contribute multiple, correlated comparisons, all relevant experimental intervention groups of the study (for example groups with yoga interventions of different intensities) will be combined into a single group and all comparable relevant control intervention groups (for example groups with exercise interventions of different intensities) will be combined into a single control group. Control groups with different types of interventions (for example waiting list control and exercise) will not be combined in a single meta-analysis but analysed separately.
Dealing with missing data
Where standard deviations are missing, they will be calculated from standard errors, confidence intervals, or t values, or attempts will be made by e-mail to obtain the missing data from the trial authors (Higgins 2011). If these data are not available, the missing standard deviation will be substituted with the mean of the standard deviations of available studies which used the same outcome scale. Where means are missing, attempts will be made by e-mail to obtain the missing data from the trial authors.
Sensitivity analyses will be conducted by excluding studies where missing data had to be substituted (see below).
The potential impact of missing data on the findings of the review will be discussed in the 'Discussion' section.
Assessment of heterogeneity
Statistical heterogeneity between studies will be assessed using the Chi2 test (Cochran 1954). A P value ≤ 0.10 will be regarded to indicate significant heterogeneity. Additionally, the I2 statistic (Higgins 2003) will be used. The magnitude of heterogeneity will be categorized as: I2 = 0% to 24%, low heterogeneity; I2 = 25% to 49%, moderate heterogeneity; I2 = 50% to 74%, substantial heterogeneity; and I2 = 75% to 100%, considerable heterogeneity.
Assessment of reporting biases
If at least 10 studies are included in a meta-analysis, funnel plots of effect estimates against their standard errors (on a reversed scale) will be generated using Review Manager software (RevMan). Publication bias will be assessed by visual analysis of funnel plots, with roughly symmetrical funnel plots indicating low risk and asymmetrical funnel plots indicating high risk of publication bias (Higgins 2011). One should be aware that funnel plot asymmetry might also arise from other sources, and that publication bias need not lead to asymmetry in the funnel plots. Further attempts will be made to avoid publication bias by searching trial registries and conference proceedings for unpublished studies.
Duplicate publication bias will be addressed as studies with more than one publication will be included only once. If there is doubt whether multiple publications refer to the same data, attempts will be made to contact the trial authors by e-mail.
Location bias will be addressed by searching multiple databases, including one of Indian journals, and by including non-English language journals.
Language bias will be avoided by including studies irrespective of the language of publication.
For continuous outcomes, data will be pooled using a random-effects model (inverse variance method). For dichotomous outcomes, a random-effects model (DerSimonian and Laird) will be used. All analyses will be performed using RevMan 5 software (RevMan).
To grade the quality of evidence, the GRADE approach will be used (Brozek 2009). The software GradePro will be used. A 'Summary of findings' table will be created to present the evidence for the primary outcomes (health-related quality, depression, anxiety, fatigue, and sleep disturbances).
Subgroup analysis and investigation of heterogeneity
Subgroup analyses will be conducted for the following.
I) Current treatment status:
women with breast cancer undergoing active cancer treatment (radiotherapy or chemotherapy);
women who have completed active treatment.
II) Time since diagnosis:
women with breast cancer diagnosed ≤ five years before time of study entry;
women with breast cancer diagnosed > five years before time of study entry.
III) Stage of cancer:
metastatic breast cancer at time of study entry;
non-metastatic breast cancer at time of study entry.
Further subgroup analyses will be conducted for the type of yoga intervention:
complex yoga interventions including physical exercise and at least one of the following: breath control, meditation, and lifestyle advice (based on yoga theory or traditional yoga practices);
exercise-based yoga interventions (based on yoga theory or traditional yoga practices) without breath control, meditation, or lifestyle advice;
meditation-based yoga interventions including at least one of the following: breath control, meditation, and lifestyle advice (based on yoga theory or traditional yoga practices) without an exercise component.
Subgroup differences will be tested using the Chi2 test for heterogeneity across subgroups. The I2 statistics for subgroup differences will be computed as the percentage of the variance between the different subgroups that is due to genuine subgroup differences rather than chance (Higgins 2011).
If statistical heterogeneity is present in the respective meta-analysis, subgroup and sensitivity analyses will also be used to explore possible reasons for the heterogeneity.
Sensitivity analyses will be performed by subsequently excluding studies with inadequate random sequence generation, studies with inadequate allocation concealment, studies without blinding of outcome assessors, and studies with high risk of attrition bias.
Further sensitivity analyses will be performed by excluding studies where missing data had to be substituted and by excluding studies that were unpublished or published only in abstract format.