Selection of studies
All abstracts identified by the search strategies described will be screened for duplicates and assessed by two independent review authors (CR and NR) to exclude studies that do not meet the inclusion criteria. Disagreements will be resolved through discussion between two review authors; in cases of persistent disagreement, a third review author will be consulted (ST). The full publications of all potentially relevant abstracts will be obtained and formally assessed for inclusion. Trials in languages different from English will be included as well. Review authors will not be blinded to the names of the study authors, their corresponding institutions, the journal of publication, or the results.
Data extraction and management
A tailored data extraction form has been developed to record the details of the studies.
Methods: study design, year, country, language, duration, sequence generation, allocation concealment, blinding.
Participants: source of participants, demographic characteristics, inclusion/exclusion criteria, numbers of participants at baseline and completion, setting.
Interventions and controls: number of arms, definitions of interventions, materials, surgical techniques, timing of surgery.
Outcomes: list of assessed outcomes, definition of each outcome, outcome assessor, blinding of the assessor.
Results: follow-up data, analyses (intention-to-treat or per-protocol), withdrawals, and losses to follow-up.
Data will be extracted independently by two review authors (LI and ST); differences of opinion between review authors will be resolved through discussion with a third review author (LM). Missing or updated information will be sought by contacting study authors.
Quantitative data from trials with more than one publication will be extracted from the latest source; this will be considered as the primary reference.
All data will be managed by using the latest version of Review Manager Software (RevMan).
Assessment of risk of bias in included studies
Two review authors will independently evaluate each study for risk of bias using the criteria recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008b) for the domains of sequence generation; allocation concealment; blinding of health professionals, participants, and outcome assessors; incomplete outcome data; selective outcome reporting; and other potential threats to validity. Each domain will be judged as having low or high risk of bias, or unclear risk of bias. We will compare the judgments and will discuss and resolve any inconsistencies in the assessments.
Sequence generation for randomization
We will assess randomization as being at low risk of bias if the procedure of sequence generation was explicitly described and is considered adequate to produce comparable groups. Examples are computer-generated random numbers, a random numbers table, and coin tossing. If no description is given, study authors will be contacted, and if no response is received, a judgment of unclear risk will be made. As per the inclusion criteria, if a response suggests that a study is at high risk of bias (ie, not randomized), it will be excluded.
We will assess concealment of treatment allocation as being at low risk of bias if the procedure was explicitly described and is considered adequate to ensure that intervention allocations could not have been foreseen in advance of, or during, enrollment. Examples are centralized randomization, numbered or coded containers, and sealed envelopes. High risk of bias procedures include alternation and references to case record numbers or dates of birth. If no description is given, study authors will be contacted; if no response is received, a judgment of unclear risk will be made. If allocation concealment has not occurred, a judgment of high risk of bias will be made.
Blinding of health professionals, participants, and outcome assessors
In this context, surgeons usually are not blinded to the surgical procedure and associated elements (eg, type of implant). The risk of bias associated with blinding of health professionals and participants will be assessed primarily on the basis of the likelihood that such blinding was sufficient to ensure that caregivers and women had no knowledge of which intervention had been received.
Even if the surgeon could not be blinded, it is possible that the health care professionals who followed participants after the procedure was performed could be blinded, and contact between other caregivers and the surgeon could be avoided. Other blinding techniques that we will evaluate are those in which participants were instructed that they should not tell outcome assessors the surgery received.
We will describe for each included study the methods used, if any, to blind the outcome assessor from knowledge of which intervention a participant received. We will judge studies to be at low risk of bias if the outcome assessors were blinded, or if we ascertain that lack of blinding may not have affected the results. If authors state that blinding was not possible because of the nature of the intervention, we will still judge the study at high risk of bias because it is possible that lack of blinding influenced the results. Blinding of health professionals will be signaled if reported.
If no description is given, study authors will be contacted, and if no response is received, a judgment of unclear risk will be made.
Incomplete outcome data
Incomplete outcome data essentially include attrition, exclusions, and missing data.
We will assign "low" risk of bias if participants included in the analysis are exactly those who were randomly assigned into the trial, and if missing outcome data are balanced in numbers across intervention groups, with similar reasons for missing data across groups, or if no outcome data are missing; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk is not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, if plausible effect size (difference in means or standardized difference in means) among missing outcomes is not enough to have a clinically relevant impact on observed effect size; or if missing data have been imputed using appropriate methods.
We will consider "high" risk of bias for any of the following: when reasons for missing outcome data are likely to be related to the true outcome, with imbalance in numbers or reasons for missing data across intervention groups; for dichotomous outcome data, when the proportion of missing outcomes compared with observed event risk is enough to induce clinically relevant bias in intervention effect estimate; for continuous outcome data, when plausible effect size (difference in means or standardized difference in means) among missing outcomes is enough to induce clinically relevant bias in observed effect size; and when "as-treated’ analysis is done with substantial departure of the intervention received from that assigned at randomization, with a potentially inappropriate application of simple imputation.
We will assign as "unclear" (uncertain risk of bias) when reporting of attrition/exclusions is insufficient to permit judgment of low or high risk of bias, or when the study did not address this outcome. Also, when the numbers randomly assigned into intervention and control groups are not clearly reported, the risk of bias is unclear.
Selective outcome reporting
We will assess reporting of outcomes as "low risk of bias" when all study outcomes declared in the Methods section have been reported in the results. We will also evaluate whether different reports of the study are available, including protocols, and will examine them to ensure that no suggestion of selective outcome reporting is made. If no description is given, study authors will be contacted, and if no response is received, a judgment of unclear will be made. If evidence suggests selective reporting, a judgment of high risk will be made.
Other potential threats to validity
We will assess other threats to validity as "low risk of bias" if the study appears to be free of other sources of bias, such as being stopped early because of a data-dependent process or having a baseline imbalance between the groups. Examples that may pose a risk of bias could include sources of sponsorship or funding.
When the risk of bias is unclear from published information, we will attempt to contact study authors for clarification. If this is not forthcoming, we will assess studies as at unclear risk of bias.
The review authors will not be blinded to the titles of journals or the identities of study authors, as they are familiar with the field. In cases of differently scored items, the two review authors will try to find agreement by discussion. A third review author will resolve any persisting disagreement.
The overall quality of evidence will be assessed using the GRADE approach (Guyatt 2008). The GRADE approach appraises the quality of a body of evidence based on the extent to which one can be confident that an estimate of effect or association reflects the item being assessed. Randomized trials start as high-quality evidence but may be downgraded because of risk of bias (methodological quality), indirectness of evidence, unexplained heterogeneity, imprecision (sparse data), and publication bias. The overall quality of the evidence for each outcome will be determined after each of these factors is considered and graded as follows.
High: Further research is very unlikely to change confidence in the estimate of effect.
Moderate: Further research is likely to have an important impact on confidence in the estimate of effect and may change the estimate.
Low: Further research is very likely to have an important impact on confidence in the estimate of effect and is likely to change the estimate.
Very low: Any estimate of effect is very uncertain.
Measures of treatment effect
Dichotomous outcomes (eg, presence/absence of infection) will be reported as risk ratios (RRs) with 95% confidence intervals (CIs). Using control event risks from the included trials, the number needed to treat for an additional beneficial outcome (NNTB) and the associated 95% confidence interval will be calculated for statistically significant dichotomous outcomes. For unwanted effects (eg, adverse events), the NNTB becomes the number needed to treat for an additional harmful outcome (NNTH) and will be calculated in the same way.
If outcome data are provided on an ordinal scale (eg, for severity of capsular contracture: minimal, moderate, severe), we will select a threshold based on the definition of clinically significant contracture and will convert these data into a dichotomous form. If it is not possible to split ordinal data into dichotomous outcomes to meet our a priori definition, we will assign a numeric score to each category and will analyze the results as continuous data.
We will calculate mean differences (MDs) of change scores if all studies use the same measurement scale. When studies use different scales, we will calculate the standardized mean differences (SMDs), using Hedges g. If necessary, we will calculate effect estimates from P values, t statistics analysis of variance (ANOVA) tables, or other statistics (Higgins 2011b).
For this analysis, we will use, according to need, either change scores or final values without combining them.
Unit of analysis issues
For each included study, we will determine whether the unit of analysis is appropriate for the unit of randomization and the design of each study (ie, whether the number of observations matches the number of "units" randomly assigned). It is unlikely that we will find cluster-randomized trials because this design is uncommon in this field. If we include a cluster-randomized trial, we will use the intraclass correlation coefficient (ICC) to convert trials to their effective sample size before incorporating them into the meta-analysis, as per the recommendation in the Cochrane Handbook for Systematic Review of Interventions (Higgins 2008c). When the ICC is not provided, we will use values for ICCs available in the published literature (Campbell 2000).
Studies with multiple treatment arms
In the primary analysis, we will combine results across all eligible intervention arms and will compare them with combined results across all eligible control arms (alternative surgical procedure), making single, pairwise comparisons. When such a strategy prevents investigation of potential sources of heterogeneity, we will analyze each surgical procedure separately (against a common control group) but will divide the sample size for common comparator arms proportionately across each comparison (Higgins 2008c). This simple approach allows the use of standard software (including RevMan) and prevents inappropriate double-counting of individuals.
Dealing with missing data
When data are missing, we will contact the corresponding authors of included studies to request any unreported data. For all outcomes in all studies, we will carry out analyses as far as possible on an intention-to-treat basis (ie, we will attempt to include all participants randomly assigned to each group in the analyses), and we will analyze all participants in the groups to which they were allocated, regardless of whether they received the allocated intervention. For continuous data that are missing, we will estimate standard deviations from other available data such as standard errors, or we will impute them using the methods suggested in Higgins 2008c. We will make no assumptions about loss to follow-up for continuous data, and we will base analyses on those participants completing the trial. If a discrepancy is noted between the number randomly assigned and the number analyzed in each treatment group, we will calculate and report the percentage lost to follow-up in each group. When it is not possible to obtain missing data, we will record this fact on the data collection form and will report it in the "Risk of bias" table; we will discuss the extent to which the missing data could alter the results/conclusions of the review. 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 analyses.
Assessment of heterogeneity
We will consider both clinical and statistical heterogeneity. If studies appear similar in terms of the level of participants, intervention type, and outcome type, we will pool the data in a meta-analysis.
Heterogeneity of effect sizes will be assessed using the I2 statistic (Higgins 2003) and the Q (Chi2) (Cochran 1954).
I2 indicates the percentage of variability due to "between-studies" (or inter-study) variability as opposed to "within-study" (or intra-study) variability.
We will interpret I2 as suggested by the latest version of Higgins 2011.
0% to 40%: might not be important.
30% to 60%: may represent moderate heterogeneity.
50% to 90%: may represent substantial heterogeneity.
75% to 100%: may represent considerable heterogeneity.
We will also evaluate the confidence interval for I2.
The Q (Chi2) statistic will be set at P < 0.10 because of the low statistical power of the test.
If statistical evidence is obtained for homogeneity of effect sizes, the analysis will use a fixed-effect model. When statistically significant heterogeneity is noted, a careful clinical review of the data will be done to find the source. The review authors will then decide (1) to redo the analysis using the homogenous subgroup (only if a clear and compelling reason to exclude the heterogeneous data can be found); (2) to abandon statistically combining the trials in favor of providing a narrative review of the literature; or (3) to redo the analysis using the random-effects model (DerSimonian 1986).
Assessment of reporting biases
We will use a funnel plot to explore bias (Egger 1997; Macaskill 2001) in the presence of at least 10 trials for our primary outcome. Asymmetry in the funnel plot of trial size against treatment effect will be used to assess this bias. We will undertake a linear regression approach as described by Egger 1997 to determine funnel plot asymmetry in the presence of at least 10 trials for the outcome.
Results will be combined unless diversity (surgical and/or statistical heterogeneity) suggests that combination is unreasonable. If both a continuous outcome and a dichotomous outcome are available for an outcome, we will include only the dichotomous outcome (ie, risk ratio [RR]) in the primary analysis. Capsular contracture rates will be summarized using risk differences if these events are found to be rare (ie, less than 10%). If some studies report an outcome as a continuous measure and others use a dichotomous measure of the same construct, we will convert results for the former from the continuous measure to a dichotomous measure, provided that we can assume a positive/negative threshold based on the definition of clinically significant contracture (otherwise, we will carry out two separate analyses). If outcomes are reported at different time points exceeding one year, data will be pooled for each point and will be combined with data from other trials at similar time points. This will lead to an estimate of the onset and persistence of treatment effect, at least over the time points available for the combination of data. A decision regarding the time points to be included in the final analysis will be made by consensus after the data have been collected.
We will calculate all overall effects using inverse variance methods, with the variance including between-study variation (ie, DerSimonian 1986 random-effects models).
We will carry out statistical analysis using Review Manager software (Review Manager 2011). We will perform meta-analyses according to the recommendations of The Cochrane Collaboration (Higgins 2011). We will conduct meta-analyses using RevMan 5 (RevMan) and will develop a "Summary of findings" table.
Subgroup analysis and investigation of heterogeneity
Subgroup analyses will be done to explore effect size differences, as follows.
Trials with low bias risk compared with trials with high bias risk.
Low-quality trials versus high-quality trials (allocation concealment vs lack of allocation concealment, blinding vs lack of blinding).
One- versus two-stage reconstruction.
Radiotherapy-treated participants versus non–radiotherapy-treated participants.
Reconstruction after breast cancer treatment versus reconstruction after risk-reducing procedures.
Early breast cancer versus locally advanced breast cancer.
We will use the "test for interaction" to identify differences between subgroups. We will use meta-regression (in the presence of adequate numbers of trials) to determine the influence of different factors on the effect estimate.
Evidence and clinical implications will be graded on the basis of the quality of the single-component approach in the following order of preference: detection bias, selection bias, and attrition bias. Discordance between data sources will be resolved using this grading system, with higher-graded studies taking precedence over lower-graded studies.
We will conduct sensitivity analyses to determine whether the findings are sensitive to restricting the analyses to studies judged to be at low risk of bias for generation of allocation sequence of the primary outcome. In addition, we will assess the sensitivity of findings to any imputed data by calculating the treatment effect while including and excluding imputed data to see whether this alters the outcome of the analysis. We will investigate the effects of dropouts and exclusions by conducting worst-case versus best-case scenario analyses.
If sensitivity analyses confirm the results of the main analysis, we will regard the results of the review with a higher degree of confidence.