Criteria for considering studies for this review
Types of studies
We will include randomised and quasi-randomised (method of allocating participants to a treatment that is not strictly random, e.g. by date of birth) controlled clinical trials evaluating WBC for prevention and treatment of muscle soreness after exercise in adults.
Types of participants
No restrictions will be placed on gender or on type or level of exercise. All field- and laboratory-based (including eccentric) exercise modalities will be included. Studies focusing on children (< 18 years of age) or injured participants will be excluded. We anticipate that people with vascular problems, such as Raynaud’s disease, who are contraindicated for cryotherapy, will be excluded from trials.
Types of interventions
At least one group in the trial will comprise participants treated with whole-body cryotherapy before or after exercise. WBC will be defined as exposure of the body (trunk, arms and legs) to extremely cold dry air (below -100°C). These exposures can be administered as a once-off treatment, or they can be repeated several times on the same days or over several days.
Consistent with the logic model included in this protocol, comparisons can be made with any other form of intervention designed to prevent or treat DOMS, including, but not limited to, passive interventions (rest, no treatment or placebo treatment), cold water immersion (immersion in water colder than 15°C), warm water immersion (immersion in water warmer than 15°C), contrast water immersion (alternating hot and cold water immersion), cool-down, stretching, massage and compression garments. Studies comparing different durations or dosages of WBC will be included. Trials in which the same WBC protocol is used in both arms as a co-intervention will not be included. Comparisons with pharmacological interventions will be excluded.
Types of outcome measures
Muscle soreness (e.g. pain measured with the use of visual analogue scales and algometer data)
Subjective recovery (return to previous activities without signs or symptoms)
Immediate or long-term complications or adverse effects (e.g. frost bite, adverse cardiac or vascular events, musculoskeletal injury)
We will collect cost and resource data, including cost of the intervention and cost of time off work or professional sports activity.
Timing of outcome assessment
We plan to collect data at the following follow-up times: immediately and 24, 48, 72, 96 and more than 96 hours post intervention. These are typical follow-up times for studies assessing treatment for DOMS.
Search methods for identification of studies
We will search the Cochrane Bone, Joint and Muscle Trauma Group Specialised Register, the Cochrane Central Register of Controlled Trials (to present), MEDLINE (1946 to present), EMBASE (1974 to present), Cumulative Index to Nursing and Allied Health (CINAHL) (1982 to present), British Nursing Index and archive (BNI) (1985 to present) and the Physiotherapy Evidence Database (PEDro) (1929 to present).
In MEDLINE, the subject-specific search will be combined with the sensitivity- and precision-maximising version of the Cochrane Highly Sensitive Search Strategy for identifying randomised trials (Lefebvre 2011). This strategy will be modified for use in other databases (see Appendix 1 for the MEDLINE search strategy).
We will also search Current Controlled Trials and the WHO International Clinical Trials Registry Platform for ongoing and recently completed trials.
We will apply no language restrictions.
Searching other resources
The reference lists of relevant articles will be searched in addition to the table of contents of the following journals not registered as being handsearched by the Cochrane Collaboration.
(Australian) Journal of Science and Medicine in Sport (1998 to present).
British Journal of Sports Medicine (1964 to present).
Clinical Journal of Sport Medicine (1991 to present).
International Journal of Sports Medicine (2005 to present).
Journal of Applied Physiology (1948 to present).
Journal of Sports Medicine and Physical Fitness (1998 to present).
Journal of Sports Sciences (1985 to 1987; 1990 to 1991; 1994; 1996; 2000 to present).
Medicine and Science in Sports and Exercise (1980 to present).
Physical Therapy in Sport (2000 to 2002; 2007 to present).
We will also search the conference proceedings of the following organisations.
American College of Sports Medicine (1986 to present) (in Medicine and Science in Sports and Exercise).
American Physical Therapy Association (1980 to present) (in Physical Therapy).
British Association of Sport and Exercise Medicine (BASEM) (1964 to present) (in British Journal of Sports Medicine).
British Association of Sport and Exercise Sciences (BASES) (1964 to present) (in Journal of Sports Sciences).
World Confederation for Physical Therapy (2003, 2007, 2011) (CD-ROM).
Data collection and analysis
Selection of studies
Two review authors (JTC, GMM) will independently select trials for inclusion. First, we will screen titles and abstracts of publications obtained by the search strategy and will remove only those that are obviously outside the scope of the review. We will be over-inclusive at this stage and will seek the full text for any papers that might meet the review inclusion criteria. We will aim to link together multiple publications and reports of the same study. The same two review authors will then independently select trials using a standardised form to record their choices. We will not be blinded during this process with respect to authors’ names, journal or date of publication. When possible, translation of non–English language studies will be undertaken. Primary authors will be contacted when necessary to ask for clarification of study characteristics. Disagreement between the review authors will be resolved by consensus or by third party adjudication (CB, PRAB, IBS).
Data extraction and management
Two review authors (JTC, CB) will use a customised form to independently extract relevant data on methodology, eligibility criteria, interventions (including detailed characteristics of the exercise protocols and the whole-body cryotherapy protocol employed), comparisons and outcome measures. Details of the characteristics of included participants such as training status, age, sex and health status will also be recorded. When available, we will also extract data on participant subgroups, including any equity considerations such as ethnicity and socioeconomic status. Any included study written by one of the current review authors will be reviewed by review authors who did not participate in the original study. Any disagreement will be resolved by consensus or by third party adjudication (GMM, PRAB). Primary authors will be contacted to clarify any omitted data or study characteristics. For intention-to-treat analysis, data will be extracted according to the original allocation groups, and losses to follow-up will be noted when possible.
Assessment of risk of bias in included studies
Two review authors (JTC, CB) will independently assess risk of bias using the tool described (and the criteria outlined) in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). To minimise bias in the interpretation of this scale, two review authors (JTC, CB) will initially assess a small sample of unrelated studies (not included in the current review); disparities in risk of bias judgements will be reviewed and discussed before any of the included studies is evaluated.
Each study will be graded for risk of bias in each of the following domains: sequence generation, allocation concealment, blinding (participants and intervention providers; outcome assessment), incomplete outcome data and selective outcome reporting. Two other sources of bias will be considered on the basis of the following questions: (1) Was the exercise protocol clear and consistent between groups? (2) Were co-interventions used, and if so, were they standardised across groups? For each study, the information pertaining to each of the domains will be described as reported in the published study report (or, if appropriate, based on information from related protocols or published comments or after discussion with the relevant authors) and the associated risk of bias judged by the review authors. Studies will be assigned 'high risk', 'low risk' or 'unclear risk' when there is uncertainty or when information is insufficient to allow review authors to make a judgement. Disagreements between review authors regarding the risk of bias assessment will be resolved by consensus.
Measures of treatment effect
For each study, risk ratios and 95% confidence intervals will be calculated for dichotomous outcomes, and mean differences and 95% confidence intervals for continuous outcomes. For continuous outcomes that are pooled on different scales, standardised mean differences will be used. When possible, follow-up scores will be used in preference to change scores.
Unit of analysis issues
If trials include data from a cluster-randomised study design, the data will be adjusted for clustering when possible. It is possible that studies will include repeated observations of the same outcome; consequently we will extract data at clinically relevant time points. When available, the following time points will be included: immediately after the exercise, immediately after the intervention and then at 24-hour intervals (0 to 24 hours, 25 to 48 hours, 49 to 72 hours, 73 to 96 hours and over 96 hours).
Dealing with missing data
In cases where data are missing, we will consider why they are missing. Whenever possible, we will contact study authors to request missing data or to ask for an explanation as to why data are missing. Unless missing standard deviations can be derived from confidence intervals, standard errors or exact P values, we will not assume or impute values for these in order to present results in the analyses.
Assessment of heterogeneity
Assessment of heterogeneity between comparable trials will be evaluated visually with the use of forest plots, as well as Chi² tests and I² statistics. The level of significance for the Chi² test will be set at P = 0.1 (Deeks 2011): a P value for Chi² < 0.1 will be considered to indicate statistically significant heterogeneity between studies. Values of I² will be interpreted as follows: 0% to 40% might not be important; 30% to 60% may represent moderate heterogeneity; 50% to 90% may represent substantial heterogeneity; and 75% to 100% may represent considerable heterogeneity.
Assessment of reporting biases
We will be vigilant in watching for duplicate publications of the same studies. Funnel plots of the effect estimates against standard error (on a reversed scale) will be created using Review Manager (RevMan 2011); these will be used to assess reporting bias when 10 or more trials are included in a comparison. Standard errors will be plotted on the vertical scale. Effect estimates will therefore be plotted on the horizontal scale, with continuous data represented as standardised mean differences, and dichotomous data represented as risk ratios on a logarithmic scale.
When considered appropriate, results of comparable groups of trials will be pooled using both fixed-effect and random-effects models. The choice of the model to report will be guided by careful consideration of the extent of heterogeneity and whether it can be explained, in addition to other factors, such as the number and size of included studies. Ninety-five per cent confidence intervals will be used throughout. We will consider not pooling data when considerable heterogeneity (I² > 75%) that cannot be explained by the diversity of methodological or clinical features is observed among trials. When it is inappropriate to pool data, we will still present trial data in the analyses or tables for illustrative purposes and will report them in the text.
Subgroup analysis and investigation of heterogeneity
When data allow, we intend to perform the following subgroup analyses.
Gender (male versus female)
Exposure dose (single versus repeated exposures; short versus long exposure durations)
Exercise type (normal sporting activities and laboratory-induced DOMS)
Training status (elite versus recreational)
We have chosen these subgroup analyses because gender, type of athletic activity and training status may impact the severity of DOMS experienced after exercise (Howatson 2008; McGinley 2009). In particular, DOMS may be augmented in untrained males after eccentric exercise when compared with trained females performing concentric exercise. Moreover, reductions in tissue temperature may be more pronounced after repeated, or longer, WBC exposures (Costello 2012c). We will investigate whether the results of subgroups are significantly different by inspecting the overlap of confidence intervals and by performing the test for determining subgroup differences that is available in Review Manager (RevMan 2011).
If some of the included trials are at high risk of bias for one or more domains, we will perform sensitivity analysis to determine whether inclusion of such trials significantly influences the effect size. We will consider trials at high risk of bias in sensitivity analysis if allocation concealment is unclear or at high risk of bias, or if attrition is greater than 20%. We will also carry out sensitivity analysis to explore the effects of using fixed-effect or random-effects analyses for outcomes with statistical heterogeneity and the effects of any assumptions made, such as the value of the intracluster correlation coefficient used for cluster-randomised trials.
Summary of findings table
We will prepare a 'Summary of findings' table for each of the main comparisons using the GRADE profiler (Schünemann 2011). We will summarise the quality of evidence by applying the principles of the GRADE framework and following the recommendations and worksheets of Cochrane Effective Practice and Organisation of Care Group for creating 'Summary of findings' tables (EPOC 2011). Thus, we will use four levels of quality (high, moderate, low and very low) to describe the body of evidence.