Criteria for considering studies for this review
Types of studies
We will include all randomised controlled trials (RCTs) of any intervention (except for quinine (see Background) for leg cramps in pregnancy. Cluster-randomised studies will be considered as mentioned in the Unit of analysis issues. Quasi-RCTs will be excluded due to obvious selection bias. Cross-over studies will also be excluded.
Types of participants
Pregnant women who are experiencing leg cramps in pregnancy. However, pregnant women with leg cramps secondary to another disease (e.g. amyotrophic lateral sclerosis, hypothyroidism), receiving medication (e.g. diuretics), undergoing haemodialysis and pregnant women with restless legs syndrome will be excluded.
Types of interventions
We will include all interventions for leg cramps in pregnancy, including:
drug/electrolyte/vitamin therapies, for example, calcium salts, magnesium salts, sodium salts, vitamins (vitamin D, vitamin E) and mineral supplements compared with placebo or no treatment. We will exclude quinine for its known adverse effects;
non-drug therapies, for example, muscle stretching, massage, relaxation, heat therapy, dorsoflexion of the foot compared with placebo or no treatment.
Types of outcome measures
1. Frequency of leg cramps, measured as the number of leg cramps per week.
1. Adverse outcomes:
maternal side effects (e.g. nausea, vomiting, diarrhoea, constipation);
labour outcome (e.g. mode of birth);
pregnancy complications (e.g. hypertension, pre-eclampsia, antepartum haemorrhage);
pregnant outcomes: fetal death, including spontaneous abortion (before 20 weeks' gestation), preterm labour and stillbirth;
neonatal outcomes: neonatal asphyxia, neonatal death: a baby death within 28 days of live birth;
congenital abnormalities (e.g. biochemical defects, genetic and chromosomal abnormalities).
2. Intensity of leg cramps, pain intensity measured by validated instruments.
3. Duration of leg cramps measured by seconds per leg cramp.
4. Health-related quality of life, for example, as measured by validated instruments.
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.
The Cochrane Pregnancy and Childbirth Group’s Trials 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.
We will not apply any language restrictions.
Searching other resources
We do not plan to search other resources.
Data collection and analysis
Selection of studies
Two review authors (Kunyan Zhou, Wenjuan Li) will independently assess for inclusion of all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third person (Liangzhi Xu).
Data extraction and management
We will design a form to extract data. For eligible studies, at least two review authors (Kunyan Zhou, Wenjuan Li) will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third person (Liangzhi Xu). We will enter data into Review Manager software (RevMan 2011) and check 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 (Kunyan Zhou, Jing Zhang) 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 assessor (Liangzhi Xu).
(1) Random sequence generation (checking for possible selection bias)
We will describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We will assess 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 assess 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 assess the methods as:
low, high or unclear risk of bias for participants;
low, high or unclear risk of bias for personnel;
low, high or unclear risk of bias for outcome assessors.
(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 assess 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 assess methods as:
low risk of bias (e.g. no missing outcome data; less than 20% 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 assess 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 assess 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 data, we will present results as summary risk ratio with 95% confidence intervals.
For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
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 are unlikely to be a valid study design for this topic and will be excluded.
Other unit of analysis issues
Multiple pregnancies studies
If we include studies involving women with multiple pregnancies, we will treat the infants as independent and note effects of estimates of confidence intervals in the review.
If we include studies using one or more treatment groups (multi-arm studies), where appropriate, we will combine groups to create a single pair-wise comparison. We will use methods described in the Handbook (Higgins 2011) to ensure that we do not double count participants.
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 the I² is greater than 30% and either the 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 2011). 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 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% confidence intervals, 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 will plan following subgroup analyses by types of interventions.
Drug interventions/electrolytes/vitamins versus placebo or no treatment, for example, calcium versus placebo or no treatment.
Non-drug interventions versus placebo or no treatment, for example, calf muscle stretching versus placebo stretching or no treatment.
Subgroup analysis will be restricted to the primary outcome.
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2011). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.
We will carry out sensitivity analysis to explore the effects of trial quality assessed by allocation concealment and other risk of bias components, by omitting studies rated as inadequate for these components. We will also use sensitivity analysis to explore the effects of fixed-effect or random-effects analysis for outcomes with statistical heterogeneity and the effects of any assumptions made. Sensitivity analysis will be restricted to the primary outcome.