Criteria for considering studies for this review
Types of studies
All published, unpublished and ongoing randomised controlled trials (including cluster-randomised trials) comparing outcomes between women given terbutaline pump maintenance therapy and controls given alternative therapy, placebo, or no therapy after successful arrest of threatened preterm labour. We will not include studies where allocation to groups is not truly random (e.g. allocation by day of the week).
We will include trials reported in abstracts if results are reported by randomisation group and provided sufficient information is reported (or can be obtained from the authors) to allow us to assess risk of bias.
Types of participants
Singleton or multifetal pregnant women with intact membranes who have had at least one episode of threatened preterm labour that was halted by tocolytic therapy.
Types of interventions
Terbutaline pump maintenance therapy compared with alternative drug therapy, placebo, or no therapy.
Types of outcome measures
Reduction in serious neonatal morbidity and mortality.
Preterm birth less than 37 completed weeks.
Very preterm birth (less than 34 completed weeks).
Extremely preterm birth (less than 28 completed weeks).
Respiratory distress syndrome.
Need for mechanical ventilation.
Neurological sequelae (general intelligence, hearing, vision, cerebral palsy and disability).
Admission to neonatal intensive care unit.
Cardiovascular complications (death, cardiac arrest, myocardial infarction, arrhythmia, hypotension).
Other serious complications (pulmonary oedema, hepatitis).
Side effects (chest pain, palpitations, shortness of breath, hyperglycaemia, hypokalaemia).
Maternal compliance with therapy.
Maternal satisfaction of therapy.
Breastfeeding at hospital discharge.
Rehospitalisation for threatened preterm labour.
Cost effectiveness of treatment.
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 search 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.
Searching other resources
We will review citations of reference lists of included papers identified through the above search strategy and assess their suitability for inclusion in the review.
We will not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors (Saifon Chawanpaiboon (SC) and Usanee Sangkomkamhang (US)) will independently assess for inclusion 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 the third author (Pisake Lumbiganon (PL)).
Data extraction and management
We will design a form to extract data. For eligible studies, two review authors (SC and US) will extract the data using the agreed form. We will resolve discrepancies through discussion with a third review author (Malinee Laopaiboon (ML)). We will enter data into Review Manager software (RevMan 2012) and check them 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
Three review authors (SC, ML and PL) 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.
(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.
(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; 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 Cochrane 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 included only parallel individual randomised controlled trials in this review. The unit of analysis will be women.
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 Cochrane Handbook (Higgins 2011) 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 subgroup analysis to investigate the effects of the randomisation unit.
Cross-over trials are not a suitable design for this type of intervention and will not be included.
Other unit of analysis issues
If we include any trials with more than two arms (multi-arm trials), we will include data for all arms relevant to the scope of the review. Where appropriate, we will combine arms (using methods described in the Cochrane Handbook (Higgins 2011)) to create a single pair-wise comparison. If it is not appropriate to combine arms, we will present results separately for each arm, sharing results for the control group between each to avoid double counting (for dichotomous outcomes we will divide the number of events and total sample by two, for continuous outcomes we will assume the same mean and standard deviation but halve the control sample size for each comparison).
We will include studies recruiting women with multiple pregnancies. We are aware that in multiple pregnancies outcomes for neonates are not independent; where sufficient information is available we will therefore adjust data for multiple pregnancies using the methods described in the Cochrane Handbook (Higgins 2011).
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 the T² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity. If we identify substantial heterogeneity, we will explore it by pre-specified subgroup analysis (see below).
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 2012). 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 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. 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.
Subgroup analysis will be restricted to the review's primary outcomes.
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2012). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.
To test the robustness of results, we plan to use sensitivity analyses to examine the effect of including studies at high risk of bias (such as from lack of allocation concealment) on the overall estimates of effect for primary outcomes.
We will use the GRADE system to define the quality of evidence in a 'Summary of findings' table, following guidance in the Cochrane Handbook (Higgins 2011).