Criteria for considering studies for this review
Types of studies
Randomised controlled trials (including those using a cluster-randomised design) comparing CAM, alone or associated with other forms of pain relief, versus other treatments or placebo or no treatment, in the treatment of post-CS pain. Quasi–randomised studies will be eligible for inclusion. Studies using a cross-over design will not be eligible for inclusion. Studies available only in abstract form will not be included in the review.
Types of participants
Women in the postpartum period after a CS.
Types of interventions
All types of CAM according to the WHO criteria (Committee CAM 2005; WHO 2001; WHO 2002; WHO 2005b), including acupuncture, aromatherapy, massage, music therapy and TENS for the treatment of postoperative pain in women submitted to CS. We will compare the following.
CAM versus placebo.
CAM versus no treatment.
CAM plus analgesia versus placebo plus analgesia.
CAM plus analgesia versus analgesia.
Types of outcome measures
Pain measured by validated instrument or scoring system (such as the visual analogue scale) up to discharge
Adverse effects (worsening of pain, anxiety, backache, pruritus, sedation)
Rescue analgesic requirement
Length of hospitalisation
Breasfeeding at discharge
Interaction with the baby
Walking at discharge
Pain at six weeks after discharge
Search methods for identification of studies
We will contact the Trials Search Co-ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register.
This register is maintained by the Trials Search Co-ordinator and contains trials identified from:
monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
weekly searches of MEDLINE;
weekly searches of Embase;
handsearches of 30 journals and the proceedings of major conferences;
weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and Embase, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co-ordinator searches the register for each review using the topic list rather than keywords.
In addition, we will contact the Cochrane Complementary Medicine Field for a search of their Trials Register.
Searching other resources
We will check reference lists of the included studies manually to identify any additional studies. We will contact specialists in the field and authors of the included trials for unpublished data.
We will not apply any language restrictions.
Data collection and analysis
The data collection and analysis methods in this section are based on the Cochrane Pregnancy and Childbirth Group's standard methods text.
Selection of studies
After merging the search results and removing duplicate records, two review authors (Sandra Zimpel (SAZ) and Gustavo Porfírio (GP)) will independently screen the references identified by the literature search. Titles and abstracts will be assessed to select potentially relevant reports which will be retrieved for full text reading. We will retrieve and examine the full text of selected studies for compliance with eligibility criteria. The reason for exclusion of individual trials will be documented. A third author (Maria Torloni (MRT)) will be consulted in case any disagreements arise during this process. We will present the process of study identification and selection using the PRISMA flow chart diagram.
Data extraction and management
We will create a specific data abstraction form to extract relevant information from each of the included studies. Two review authors (SAZ, GP) will independently extract the data using this form. We will resolve discrepancies through discussion or, if required, we will consult a third author (MRT). We will enter data into Review Manager software (RevMan 2014) and check it for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors (SAZ, GP) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a third author (MRT).
(1) Random sequence generation (checking for possible selection bias)
We will describe for each included study the method used to generate the allocation sequence and assess whether it was reported in sufficient detail to allow an assessment of whether it should produce comparable groups.
We will categorise the method as:
low risk of bias (any truly random process, e.g. random number table; computer random number generator);
high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);
unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal allocation to interventions prior to assignment and will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We will categorise the methods as:
low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
high risk of bias (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);
unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.
We will categorise the methods as:
low, high or unclear risk of bias for participants;
low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.
We will categorise methods used to blind outcome assessment as:
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re-include missing data in the analyses which we undertake.
We will categorise methods as:
low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);
unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We will categorise the methods as:
low risk of bias (where it is clear that all of the study’s pre-specified outcomes and all expected outcomes of interest to the review have been reported);
high risk of bias (where not all the study’s pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
We will describe for each included study any important concerns we have about other possible sources of bias.
We will categorise whether each study was free of other problems that could put it at risk of bias:
(7) Overall risk of bias
We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous variables, we will calculate the risk ratio (RR) and 95% confidence intervals (CIs) .
For continuous data, mean differences (MD) and 95% CIs between treatment groups will be calculated if studies report exactly the same outcomes. If similar outcomes are reported on different scales, the standardised mean difference (SMD) and 95% CI will be calculated.
For time-to-event data, since the most appropriate way of summarising them is to use methods of survival analysis and express the intervention effect as a hazard ratio, these data will be taken directly from the results of the studies. If estimates of log hazard ratios and standard errors can be obtained from results of the studies, these data will be combined using the generic inverse-variance method (Higgins 2011).
Unit of analysis issues
The unit of analysis is based on the individual participant (unit to be randomised for interventions to be compared), i.e. the number of observations in the analysis should match the number of individuals randomised. In the case of studies with multiple intervention groups, we will combine groups to create a single pair-wise comparison, combining all relevant intervention or control groups into a single group (Higgins 2011).
We will include cluster-randomised trials in the analyses along with individually-randomised trials. We will adjust their sample sizes using the methods described in the Handbook using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster-randomised trials and individually-randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.
We will also acknowledge heterogeneity in the randomisation unit and perform a subgroup analysis to investigate the effects of the randomisation unit.
Cross-over trials will not be eligible for inclusion.
Dealing with missing data
For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.
For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat basis, i.e. we will attempt to include all participants randomised to each group in the analyses, and all participants will be analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial will be the number randomised minus any participants whose outcomes are known to be missing.
Assessment of heterogeneity
We will assess statistical heterogeneity in each meta-analysis using the T², I² and Chi² statistics. We will regard heterogeneity as substantial if an I² is greater than 30% and either a T² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
If there are 10 or more studies in the meta-analysis, we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually. If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.
We will carry out statistical analysis using the Review Manager software (RevMan 2014). We will use fixed-effect meta-analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random-effects meta-analysis to produce an overall summary, if an average treatment effect across trials is considered clinically meaningful. The random-effects summary will be treated as the average of the range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.
If we use random-effects analyses, the results will be presented as the average treatment effect with 95% CIs, and the estimates of T² and I².
Subgroup analysis and investigation of heterogeneity
If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random-effects analysis to produce it.
We plan to carry out the following subgroup analyses:
multiparous versus primiparous women;
first caesarean versus repeat caesarean;
elective caesarean versus emergency caesarean.
Subgroup analysis will be restricted the review's primary outcomes.
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.
If there are an adequate number of studies, sensitivity analyses will be performed based on separation of studies according to risk of bias analysing the effect of trial quality in the primary outcomes. This will be done by excluding the trials most susceptible to bias based on our 'Risk of bias' assessment, i.e., those with inadequate randomisation sequence generation, allocation concealment, high levels of post-randomisation losses or exclusions and uncertain or unblinded outcome assessment (Deeks 2001). We will also carry out sensitivity analysis for primary outcomes by removing quasi-randomised trials to examine the effect of excluding such trials.