Atención entre embarazos a pacientes con antecedentes de diabetes gestacional para mejorar los resultados maternos y del recién nacido
Appendices
Appendix 1. Methods of data collection and analysis to be used in future updates of this review
Data collection and analysis
The following methods of data collection and analysis are based on Cochrane Pregnancy and Childbirth standard methods text template.
Selection of studies
Two review authors 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 a third author.
Data extraction and management
We will design a form to extract data. For eligible studies, two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult the third author. We will enter data into Review Manager software (RevMan 2014) and check the data 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 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.
(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:
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low risk of bias (any truly random process, e.g. random number table; computer random number generator);
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high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number); or
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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:
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low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
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high risk of bias (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth); or
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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:
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low, high or unclear risk of bias for participants; and
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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:
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low, high or unclear risk of bias.
(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:
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low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
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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); or
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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:
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low risk of bias (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported);
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high risk of bias (where not all the study’s prespecified outcomes have been reported; one or more reported primary outcomes were not prespecified; 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); or
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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.
(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.
Assessment of the quality of the evidence using the GRADE approach
We will assess the quality of the evidence using the GRADE approach as outlined in the GRADE handbook in order to assess the quality of the body of evidence relating to the following outcomes for the main comparison. We will use the Cochrane Pregnancy and Childbirth GRADE core outcome set for reviews of prevention and treatment of gestational diabetes mellitus (GDM) and pre‐existing diabetes in pregnancy, adapted for this review question.
For women
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Gestational diabetes mellitus (GDM) (diagnostic criteria as defined in individual trials)
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Hypertensive disorders of pregnancy (including pre‐eclampsia, pregnancy‐induced hypertension, eclampsia)
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Caesarean section
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Perineal trauma
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Weight gain
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Postnatal depression
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Type 2 diabetes mellitus
For children
Fetuses/neonates
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Large‐for‐gestational age
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Perinatal mortality (stillbirth or neonatal death)
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Mortality or morbidity composite (e.g. death, shoulder dystocia, bone fracture or nerve palsy)
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Hypoglycaemia
Children/adults
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Adiposity (e.g. as measured by body mass index (BMI), skinfold thickness)
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Type 2 diabetes mellitus
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Neurosensory disability
We will use the GRADEpro Guideline Development Tool to import data from Review Manager 5.3 (RevMan 2014) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes will be produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.
Measures of treatment effect
Dichotomous data
For dichotomous data, we will present results as summary risk ratios (RRs) with 95% confidence intervals (CIs).
Continuous data
For continuous data, we will use the mean difference (MD) if outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
Cluster‐randomised trials
We will include cluster‐randomised trials in the analyses along with individually‐randomised trials. We will adjust their sample sizes or standard errors using the methods described in the Cochrane Handbook using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), or from another source (Higgins 2011). If ICCs from other sources are used, 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 separate meta‐analysis.
Cross‐over trials
We will exclude cross‐over trials from this review.
Multi‐armed trials
Where a multi‐armed trial is included, we will record and include all outcome data in the review as two‐arm comparisons. We will include the data for the different arms in independent two‐arm comparisons in separate meta‐analyses. In instances where we cannot include the data in separate comparisons, we will combine it to create a single pair‐wise comparison (Higgins 2011). If the control group is shared by two or more study arms, we will divide the control group between relevant subgroup categories to avoid double‐counting the participants (for dichotomous data we will divide the events and the total population, while for continuous data we will assume the same mean and standard deviation (SD) but will divide the total population). We will describe the details in the 'Characteristics of included studies' tables.
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.
We will carry out all outcome 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. 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 Tau², I² and Chi² statistics. We will regard heterogeneity as substantial if an I² is greater than 30% and either a Tau² 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.
Data synthesis
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, we will present the results as the average treatment effect with 95% CIs, and the estimates of Tau² 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.
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Periconceptual BMI (e.g. underweight versus normal range versus overweight versus obese versus morbidly obese).
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Polycystic ovarian syndrome (yes versus no).
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Diagnostic criteria for GDM in previous pregnancy (e.g. International Association of Diabetes and Pregnancy Study Groups criteria (IADPSG 2010) versus other).
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Management of GDM in previous pregnancy (e.g. non‐pharmacological measures (dietary and lifestyle advice) versus oral anti‐diabetic agents versus insulin).
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Ethnicity (e.g. high risk versus low risk).
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Pregnancy interval (e.g. estimated date of delivery less than one year from last birth versus one year to five years from last birth versus more than five years from last birth).
We will restrict subgroup analyses to the review's primary outcomes.
We will assess differences between subgroups by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.
Sensitivity analysis
We plan to carry out sensitivity analysis on primary outcomes to explore the effect of trial quality where there is an overall high risk of bias associated with included trials or where quasi‐randomised or cluster‐randomised trials are included in the review. We will consider a study to be at overall high risk of bias if both concealment of allocation and attrition rates are assessed as being at high risk of bias. We plan to exclude studies of poor quality from the analysis (those rating as high risk in total overall risk of bias) or quasi‐randomised or cluster‐randomised trials in order to assess for any substantive difference in the overall result.
Study flow diagram.
