Yoga treatment for chronic non-specific low-back pain
Background
Description of the condition
Low-back pain, defined as pain or discomfort in the area between the lower rib and the gluteal folds, is a common, potentially disabling condition (Koes 2006). The 3-month prevalence of low-back pain is estimated at 25%, and lifetime prevalence has been estimated to be as high as 84% (Deyo 2006; Balague 2012; Hoy 2012). Low-back pain is associated with loss of work productivity, poor quality of life, and high medical expenses, and is a substantial economic burden on society (Deyo 2006; Dagenais 2008).
Back pain is sometimes associated with a likely etiology (e.g., radiculopathy or spinal stenosis), but the vast majority of low-back pain cases are of unknown origin and are classified as non-specific (van Tulder 1997). Low-back pain may also be classified according to the duration of pain as acute (less than 4 weeks), subacute (between 4 weeks and 3 months), or chronic (3 months or greater) (van Tulder 2006; Chou 2007). Most episodes of low back pain are mild (Cassidy 2005) and activity limitations are rare (Lawrence 2008). Symptoms often improve during the first six weeks (Costa 2012; Buchbinder 2012). A small subset of chronic and severe cases is responsible for much of the disability and related medical costs due to low-back pain (Luo 2004). Low-back pain is an intermittent and recurring condition. Among individuals with a resolved episode of low-back pain, it is estimated that between 24% and 74% will have a recurrent episode within one year (Pengel 2003; Stanton 2008).
The usual treatment for low-back pain is self-care and over-the-counter medication such as acetaminophen or non-steroidal anti-inflammatory drugs. For chronic low-back pain, current guidelines list exercise therapy and massage among the therapies that may be beneficial (Chou 2007). However, the current evidence does not provide guidance on selecting one treatment approach over another, or when specific treatments are warranted, and the best treatment approaches remain unclear (Haldeman 2008), while many treatments are costly and of unclear effectiveness (Deyo 2009).
Description of the intervention
Yoga is a mind-body practice originating from ancient India which has also become popular in the West over the last century (Saper 2004). There are many branches and styles of yoga practice, with varying philosophies and practices, but all may be characterized by the integration of physical poses (asanas) and controlled breathing (pranayama), and frequently also the incorporation of meditation (dhyana) (Hewitt 2001; Hayes 2010; Yoga Alliance 2012). According to the 2007 National Health Interview Survey, the use of yoga in the United States increased between 2002 and 2007, and in 2007 over 13 million adults had used yoga during the previous year (Birdee 2008;Barnes 2008).
Therapeutic yoga is the use of yoga to help people with health problems manage their condition and reduce their symptoms (Yoga Alliance 2012). Yoga has been suggested as being useful in managing pain and associated disability across a range of conditions, including back pain (McCall 2007; Bussing 2012). In the 2002 National Health Interview Survey (NHIS) Alternative Medicine Supplement survey over 10 million U.S. adults described using yoga for health reasons; 10.5% of yoga users said that their use was for musculoskeletal conditions and 76% of these users reported that the yoga was helpful (Birdee 2008).
How the intervention might work
A range of potential benefits has been proposed in relation to the practice of yoga in persistent pain conditions, which include changes in physiological, behavioral and psychological factors (Wren 2011). Potential mechanisms for these changes include improved flexibility and muscular strength derived from practicing the physical poses of yoga, increased mental and physical relaxation derived from practicing controlled breathing or meditation exercises, and improved body awareness gained through both the physical and mental aspects of yoga (Sorosky 2008; Daubenmier 2012).
Why it is important to do this review
Yoga is one of several complementary therapies often used to treat low-back pain, and in surveys patients frequently report that it is helpful (Wolsko 2003; Birdee 2008). Several recent randomized controlled trials (RCTs) have tested the effectiveness of yoga in relieving the symptoms of low-back pain. Since yoga is a commonly used therapy for a highly prevalent, recurrent and bothersome health problem for which there are no clearly satisfactory treatments, and recent large RCTs are available, it is important to critically evaluate the current evidence for yoga as a treatment for low-back pain.
Objectives
To assess the effects of yoga for treating chronic non-specific low-back pain, compared to no specific treatment, a minimal intervention (e.g., education), or another active treatment, with a focus on both pain and function.
Methods
Criteria for considering studies for this review
Types of studies
We will include randomized controlled trials (RCTs) with clearly reported and appropriate randomization. If the study report does not include a clear description of the method of randomization, we will contact the authors for information on the method of randomization to confirm that the trial was adequately randomized. We will exclude quasi-randomized trials. We will not restrict study eligibility by language or publication status.
Types of participants
We will include trials in adults (aged 18 years or greater) with current chronic non-specific low-back pain. In our description of population and setting, we will specify whether the participants were recruited from populations seeking medical care or from the community.
Types of interventions
We will include studies of yoga as an intervention for low-back pain. The study must specify that the intervention was 'yoga'. We will exclude interventions based upon yoga (e.g., stretching exercises based upon yoga) but not characterized as yoga. We will not restrict studies according to the yoga tradition used, or according to the dose, frequency or duration of the yoga intervention. However, we will exclude studies examining meditation or a yoga lifestyle without a physical practice component.
We will include studies comparing yoga to any other intervention or to no intervention. We will also include any studies comparing yoga as an adjunct to other therapies, versus those other therapies alone. The comparisons of interest will be:
- Yoga versus no treatment or a waiting list;
- Yoga versus a minimal intervention (e.g., booklets);
- Yoga versus usual care;
- Yoga versus another active intervention, for which different types of active interventions are considered separately (e.g., yoga versus drugs, (and for which different types of conservative active control interventions will also be considered separately (e.g., yoga versus stretching, yoga versus manipulation)); and
- Yoga plus any intervention versus that intervention alone, for which different types of co-intervention are considered separately (e.g., yoga plus drugs versus drugs alone).
Co-interventions will be allowed, but must be comparable between intervention groups (e.g., both groups allowed the use of pain medications).
Types of outcome measures
We will use outcome measures that are considered to be important in assessment of low-back pain, so that this review may produce results that are easily compared to or combined with those of other systematic reviews of treatment for low-back pain. All outcomes will be assessed at short-term (closest to four weeks), intermediate-term (closest to six months), and long-term (closest to one year) time points.
Primary outcomes
The primary outcomes will be pain (e.g., the visual analogue scale (VAS) for pain) and back-specific functional status (e.g., the Roland Disability Questionnaire).
Secondary outcomes
The secondary outcomes will be overall measures of clinical improvement, measures of well-being (e.g., quality of life measured on the SF-36), measures of work disability, and adverse outcomes reported in the original trials.
Search methods for identification of studies
Electronic searches
We will use the Cochrane highly sensitive search strategy (Lefebvre 2011) to search the current issue of the Cochrane Central Register of Controlled Trials (CENTRAL) on The Cochrane Library, MEDLINE (from inception) (Appendix 1), EMBASE (from inception) (Appendix 2) CINAHL (from inception), PsycINFO (from inception), and AMED (from inception). We will search the Indian medical literature via the IndMED database (http://indmed.nic.in/). The Cochrane Complementary Medicine Field Specialized Register and the Cochrane Back Review Group Trials Register will also be searched. We will search the WHO International Clinical Trials Registry Platform (http://www.who.int/ictrp/search/en/) and the U.S. National Institutes of Health ClinicalTrials.gov (http://www.clinicaltrials.gov) for registered trials. We will not restrict searches by language or publication status.
Searching other resources
We will screen the reference lists of included studies and contact experts in the field (e.g., authors of included studies) for information on additional trials, including unpublished or ongoing studies.
Data collection and analysis
Selection of studies
Two authors will independently screen the titles and abstracts of references retrieved from searches. The full text will be obtained for references that either author considers relevant. Two authors will independently assess the full text references for inclusion according to the Criteria for considering studies for this review. Disagreements will be resolved by consensus or by consultation with a third author.
Data extraction and management
Two authors will use a standardized and pilot-tested form to independently extract data on study design, setting and sponsorship, study participants, components of yoga and comparison interventions, and outcomes. We will extract information on funding and sponsorship for each trial. If key information is missing from the study report, we will contact the report authors to obtain the information. Disagreements will be resolved by consensus or by consultation with a third author.
Assessment of risk of bias in included studies
Two authors will independently assess the risk of bias for each included study using the 12 'Risk of bias' items recommended by the Cochrane Back Group (Furlan 2009). These items are an adaptation of the 'Risk of bias' criteria described in theCochrane Handbook(Higgins 2011a). The description of each item and how to rate each item as 'low risk of bias', 'high risk of bias', or 'unclear risk of bias' are presented in Appendix 3. Disagreements between raters will be resolved by consensus or by consultation with a third author. We will pilot test the 'Risk of bias' assessment to ensure that raters take a similar approach to the risk of bias, and assess the interrater reliability of the assessment.
We will classify studies as having a high risk of bias if they fail to meet at least 6 of the 12 Cochrane Back Group criteria, or the study has a serious flaw (e.g., 80% drop-out rate) (Furlan 2009), and conduct a sensitivity analysis to explore the effects of including and excluding trials at high risk of bias (Sensitivity analysis).
Assessment of clinical relevance of included studies
Two authors will independently assess the clinical relevance of each included study using the five clinical relevance items recommended by the Cochrane Back Group (Furlan 2009) and listed in Appendix 4. Each question will be answered Yes, No, or Unclear, and disagreements between raters will be resolved by consensus or by consultation with a third author. We will use Cohen’s three levels to interpret the clinical importance of between-group effects. The three levels are small (standardized effect size < 0.5), medium (standardized effect size from 0.5 to < 0.8), and large (standardized effect size ≧ 0.8) (Cohen 1988; Furlan 2009). The answers to the clinical relevance items will be used to inform the discussion of the clinical relevance of the review conclusions.
Measures of treatment effect
We will analyze dichotomous outcomes by calculating the relative risk (RR). We will analyze continuous outcomes by calculating the mean difference (MD) when the same instrument is used to measure outcomes, or the standardized mean difference (SMD) when different instruments are used to measure the outcomes and the instruments measure the same underlying construct (e.g., pain). We will express the uncertainty with 95% confidence intervals (95% CI) for all estimates.
Unit of analysis issues
We do not expect that cluster-randomized or cross-over trials have been carried out in yoga for low-back pain. However, if we identify cluster-randomized or cross-over trials, we will follow the guidance in chapters 16.3 and 16.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b) in assessing their suitability and including them in the analysis if appropriate.
Dealing with missing data
The first author or primary investigator will be contacted for trials in which data for key study characteristics or primary outcomes are missing or incomplete. In cases where study participants are lost to follow-up, and intention-to-treat analyses are conducted using imputation alongside available case analyses, we will use the imputed data for our primary analysis, and conduct a sensitivity analysis using available case data.
Assessment of heterogeneity
Clinical heterogeneity (i.e., differences in study populations, interventions, and outcomes) between studies will be assessed qualitatively. For studies that are clinically homogenous and therefore appropriate for combining in a meta-analysis, we will assess statistical heterogeneity using the Chi2 test, for which a P value of less than 0.05 indicates statistically-significant heterogeneity.
Assessment of reporting biases
For meta-analyses in which at least 10 studies are included, we will used funnel plots to assess the potential for small study bias. We will assess the possibility of selective outcome reporting for each study as part of the 'Risk of bias' assessment.
Data synthesis
We will group the analyses separately according to the control interventions, the outcomes measured, and the timing of outcome assessment. We will combine the outcome measures from the individual trials through meta-analysis where possible (clinical comparability of population, intervention, outcomes and time of assessment between trials) using a random-effects model, because we expect some between study variation. A Chi test P value of less than 0.05 indicates statistically-significant heterogeneity.
Should the data be considered not sufficiently similar to be combined in a meta-analysis, the results from clinically comparable trials will be described qualitatively in the text.
Regardless of whether sufficient data are available to use quantitative analyses to summarize the data, we will assess the overall quality of the evidence for each comparison/outcome. To accomplish this, we will use the GRADE approach, as recommended in the Cochrane Handbook (Higgins 2011b) and adapted in the updated Cochrane Back Review Group method guidelines (Furlan 2009). Factors that may decrease the quality of the evidence are: study design and risk of bias, inconsistency of results, indirectness (not generalizable), imprecision (sparse data) and other factors (e.g. reporting bias). The quality of the evidence for a specific outcome will be reduced by a level, according to the performance of the studies against these five factors.
High quality evidence: there are consistent findings among at least 75% of RCTs with low risk of bias, consistent, direct and precise data and no known or suspected publication biases. Further research is unlikely to change either the estimate or our confidence in the results.
Moderate quality evidence: one of the domains is not met. Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate.
Low quality evidence: two of the domains are not met. Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate.
Very low quality evidence: three of the domains are not met. We are very uncertain about the results.
No evidence: no RCTs were identified that addressed this outcome
Subgroup analysis and investigation of heterogeneity
If we identify studies that test yoga interventions without a mind component (e.g., studies that test only the physical practice component of yoga and do not include meditation, relaxation, or breathing exercises), we will use subgroup analyses to evaluate the differences in outcomes between yoga interventions with and without a mind component. We will also conduct subgroup analyses of trials conducted in lower socio-economic status (SES) or lower-educated populations versus higher SES or higher-educated populations, trials conducted in older (mean age 65 or greater) versus younger populations, and trials conducted with participants who have major comorbidities (e.g., heart disease) versus trials conducted with participants who do not have these major comorbidities, if data are available. For each subgroup analysis, we will use a significance test to investigate whether the subgroup variable is associated with a statistically-significant difference in outcomes between subgroups.
Sensitivity analysis
For the primary outcomes, we will compare analyses including and excluding trials at high risk of bias (as defined in Assessment of risk of bias in included studies) in order to explore the impact of risk of bias upon estimates of trea
tment effects. We will also use sensitivity analyses to compare analyses using imputed and available case data.
Appendices
Appendix 1. MEDLINE (OvidSP) search strategy
1. randomized controlled trial.pt.
2. controlled clinical trial.pt.
3. randomized.ab.
4. placebo.ab,ti.
5. drug therapy.fs.
6. randomly.ab,ti.
7. trial.ab,ti.
8. groups.ab,ti.
9. or/1-8.
10. (animals not (humans and animals)).sh.
11. 9 not 10
12. dorsalgia.ti,ab.
13. exp back pain/
14. exp low back pain/
15. backache.ti,ab.
16. back ache.ti.
17. back pain.ti.
18. (lumbar adj pain).ti,ab.
19. coccyx.ti,ab.
20. coccydynia.ti,ab.
21. sciatica.ti,ab.
22. sciatic neuropathy/
23. spondylosis.ti,ab.
24. lumbago.ti,ab.
25. or/12-24
26. exp yoga/
27. yoga.mp.
28. asana*.mp.
29. pranayama.mp.
30. dhyana.mp
31. or/26-30
32. 11 and 25 and 31
Appendix 2. EMBASE (Ovid SP) search strategy
Based on the Back Group’s generic search for randomized controlled trials and controlled clinical trials and the specific strategy for back problems.
1 Clinical Article/
2 exp Clinical Study/
3 Clinical Trial/
4 Controlled Study/
5 Randomized Controlled Trial/
6 Major Clinical Study/
7 Double Blind Procedure/
8 Multicenter Study/
9 Single Blind Procedure/
10 Phase 3 Clinical Trial/
11 Phase 4 Clinical Trial/
12 crossover procedure/
13 placebo/
14 or/1-13
15 allocat$.mp.
16 assign$.mp.
17 blind$.mp.
18 (clinic$ adj25 (study or trial)).mp.
19 compar$.mp.
20 control$.mp.
21 cross?over.mp.
22 factorial$.mp.
23 follow?up.mp.
24 placebo$.mp.
25 prospectiv$.mp.
26 random$.mp.
27 ((singl$ or doubl$ or trebl$ or tripl$) adj25 (blind$ or mask$)).mp.
28 trial.mp.
29 (versus or vs).mp.
30 or/15-29
31 14 and 30
32 human/
33 Nonhuman/
34 exp ANIMAL/
35 Animal Experiment/
36 33 or 34 or 35
37 32 not 36
38 31 not 36
39 37 and 38
40 38 or 39
41 dorsalgia.mp.
42 back pain.mp.
43 backache.ti
44 back ache.ti
45 exp LOW BACK PAIN/
46 exp BACKACHE/
47 (lumbar adj pain).mp.
48 coccyx.mp.
49 coccydynia.mp.
50 sciatica.mp.
51 exp ISCHIALGIA/
52 spondylosis.mp.
53 lumbago.mp.
54. back disorder$.ti,ab.
55. or/41-54
56. exp yoga/
57. yoga.mp.
58. asana*.mp.
59. pranayama.mp.
60. dhyana.mp
61. or/56-60
62. 40 and 55 and 61
2 exp Clinical Study/
3 Clinical Trial/
4 Controlled Study/
5 Randomized Controlled Trial/
6 Major Clinical Study/
7 Double Blind Procedure/
8 Multicenter Study/
9 Single Blind Procedure/
10 Phase 3 Clinical Trial/
11 Phase 4 Clinical Trial/
12 crossover procedure/
13 placebo/
14 or/1-13
15 allocat$.mp.
16 assign$.mp.
17 blind$.mp.
18 (clinic$ adj25 (study or trial)).mp.
19 compar$.mp.
20 control$.mp.
21 cross?over.mp.
22 factorial$.mp.
23 follow?up.mp.
24 placebo$.mp.
25 prospectiv$.mp.
26 random$.mp.
27 ((singl$ or doubl$ or trebl$ or tripl$) adj25 (blind$ or mask$)).mp.
28 trial.mp.
29 (versus or vs).mp.
30 or/15-29
31 14 and 30
32 human/
33 Nonhuman/
34 exp ANIMAL/
35 Animal Experiment/
36 33 or 34 or 35
37 32 not 36
38 31 not 36
39 37 and 38
40 38 or 39
41 dorsalgia.mp.
42 back pain.mp.
43 backache.ti
44 back ache.ti
45 exp LOW BACK PAIN/
46 exp BACKACHE/
47 (lumbar adj pain).mp.
48 coccyx.mp.
49 coccydynia.mp.
50 sciatica.mp.
51 exp ISCHIALGIA/
52 spondylosis.mp.
53 lumbago.mp.
54. back disorder$.ti,ab.
55. or/41-54
56. exp yoga/
57. yoga.mp.
58. asana*.mp.
59. pranayama.mp.
60. dhyana.mp
61. or/56-60
62. 40 and 55 and 61
Appendix 3. Criteria for assessing risk of bias for internal validity (Higgins 2011a)
Random sequence generation (selection bias)
Selection bias (biased allocation to interventions) due to inadequate generation of a randomised sequence
There is a low risk of selection bias if the investigators describe a random component in the sequence generation process such as: referring to a random number table, using a computer random number generator, coin tossing, shuffling cards or envelopes, throwing dice, drawing of lots, minimisation (minimisation may be implemented without a random element, and this is considered to be equivalent to being random).
There is a high risk of selection bias if the investigators describe a non-random component in the sequence generation process, such as: sequence generated by odd or even date of birth, date (or day) of admission, hospital or clinic record number; or allocation by judgement of the clinician, preference of the participant, results of a laboratory test or a series of tests, or availability of the intervention.
Allocation concealment (selection bias)
Selection bias (biased allocation to interventions) due to inadequate concealment of allocations prior to assignment
There is a low risk of selection bias if the participants and investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web-based and pharmacy-controlled randomisation); sequentially numbered drug containers of identical appearance; or sequentially numbered, opaque, sealed envelopes.
There is a high risk of bias if participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias, such as allocation based on: using an open random allocation schedule (e.g. a list of random numbers); assignment envelopes were used without appropriate safeguards (e.g. if envelopes were unsealed or non-opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; or other explicitly unconcealed procedures.
Blinding of participants
Performance bias due to knowledge of the allocated interventions by participants during the study
There is a low risk of performance bias if blinding of participants was ensured and it was unlikely that the blinding could have been broken; or if there was no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding.
Blinding of personnel/ care providers (performance bias)
Performance bias due to knowledge of the allocated interventions by personnel/care providers during the study
There is a low risk of performance bias if blinding of personnel was ensured and it was unlikely that the blinding could have been broken; or if there was no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding.
Blinding of outcome assessor (detection bias)
Detection bias due to knowledge of the allocated interventions by outcome assessors
There is low risk of detection bias if the blinding of the outcome assessment was ensured and it was unlikely that the blinding could have been broken; or if there was no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding, or:
- for patient-reported outcomes in which the patient was the outcome assessor (e.g. pain, disability): there is a low risk of bias for outcome assessors if there is a low risk of bias for participant blinding (Boutron 2005)
- for outcome criteria that are clinical or therapeutic events that will be determined by the interaction between patients and care providers (e.g. co-interventions, length of hospitalisation, treatment failure), in which the care provider is the outcome assessor: there is a low risk of bias for outcome assessors if there is a low risk of bias for care providers (Boutron 2005)
- for outcome criteria that are assessed from data from medical forms: there is a low risk of bias if the treatment or adverse effects of the treatment could not be noticed in the extracted data (Boutron 2005)
Incomplete outcome data (attrition bias)
Attrition bias due to amount, nature or handling of incomplete outcome data
There is a low risk of attrition bias if there were no missing outcome data; reasons for missing outcome data were unlikely to be related to the true outcome (for survival data, censoring unlikely to be introducing bias); missing outcome data were balanced in numbers, with similar reasons for missing data across groups; for dichotomous outcome data, the proportion of missing outcomes compared with the observed event risk was not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, the plausible effect size (difference in means or standardised difference in means) among missing outcomes was not enough to have a clinically relevant impact on observed effect size, or missing data were imputed using appropriate methods (if drop-outs are very large, imputation using even "acceptable" methods may still suggest a high risk of bias) (van Tulder 2003). The percentage of withdrawals and drop-outs should not exceed 20% for short-term follow-up and 30% for long-term follow-up and should not lead to substantial bias (these percentages are commonly used but arbitrary, not supported by literature) (van Tulder 2003).
Selective Reporting (reporting bias)
Reporting bias due to selective outcome reporting
There is low risk of reporting bias if the study protocol is available and all of the study's pre-specified (primary and secondary) outcomes that are of interest in the review have been reported in the pre-specified way, or if the study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were pre-specified (convincing text of this nature may be uncommon).
There is a high risk of reporting bias if not all of the study's pre-specified primary outcomes have been reported; one or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not pre-specified; one or more reported primary outcomes were not pre-specified (unless clear justification for their reporting is provided, such as an unexpected adverse effect); one or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta-analysis; the study report fails to include results for a key outcome that would be expected to have been reported for such a study.
Group similarity at baseline (selection bias)
Bias due to dissimilarity at baseline for the most important prognostic indicators.
There is low risk of bias if groups are similar at baseline for demographic factors, value of main outcome measure(s), and important prognostic factors (examples in the field of back and neck pain are duration and severity of complaints, vocational status, percentage of patients with neurological symptoms) (van Tulder 2003).
Co-interventions (performance bias)
Bias because co-interventions were different across groups
There is low risk of bias if there were no co-interventions or they were similar between the index and control groups (van Tulder 2003).
Compliance (performance bias)
Bias due to inappropriate compliance with interventions across groups
There is low risk of bias if compliance with the interventions was acceptable, based on the reported intensity/dosage, duration, number and frequency for both the index and control intervention(s). For single-session interventions (e.g. surgery), this item is irrelevant (van Tulder 2003).
Intention-to-treat-analysis
There is low risk of bias if all randomised patients were reported/analysed in the group to which they were allocated by randomisation.
Timing of outcome assessments (detection bias)
Bias because important outcomes were not measured at the same time across groups
There is low risk of bias if all important outcome assessments for all intervention groups were measured at the same time (van Tulder 2003).
Other bias
Bias due to problems not covered elsewhere in the table
There is a low risk of bias if the study appears to be free of other sources of bias not addressed elsewhere (e.g. study funding).
Appendix 4. Questions for clinical relevance
- Are the patients described in detail so that you can decide whether they are comparable to those that you see in your practice?
- Are the interventions and treatment settings described well enough so that you can provide the same for your patients?
- Were all clinically relevant outcomes measured and reported?
- Is the size of the effect clinically important?
- Were adverse effects of treatment considered, and what adverse events were reported?
- Are the likely treatment benefits worth the potential harms?
Contributions of authors
Study concept and design: L. Susan Wieland, Nicole Skoetz, Eric Manheimer, Karen Pilkington, Ramaprabhu Vempati
Development of search strategy: Karen Pilkington, L. Susan Wieland, Nicole Skoetz
Searching for studies: Karen Pilkington, L. Susan Wieland
Analysis and interpretation of data: L. Susan Wieland
Study selection: L. Susan Wieland, Nicole Skoetz, Karen Pilkington, Ramaprabhu Vempati
Data extraction: L. Susan Wieland, Nicole Skoetz, Eric Manheimer
Data analysis: L. Susan Wieland, Nicole Skoetz, Ramaprabhu Vempati
Drafting the manuscript: L. Susan Wieland
Critically revising manuscript for important intellectual content and providing final approval of the version to be published: L. Susan Wieland, Nicole Skoetz, Eric Manheimer, Karen Pilkington, Ramaprabhu Vempati, Brian Berman
Declarations of interest
None
Sources of support
Internal sources
- No sources of support supplied
External sources
- NIH National Center for Complementary and Alternative Medicine, R24 AT001293, USA.
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