Criteria for considering studies for this review
Types of studies
We will consider randomised controlled trials (RCTs) and cluster-randomised trials comparing staples with sutures in any type of surgery. We will exclude non-randomised studies.
Types of participants
Trials recruiting adults (aged 18 years or over) undergoing any type of surgical intervention in a hospital operating theatre.
Types of interventions
The interventions to be considered are staples or sutures, where these are directly compared. We will not include studies that have used any other material (e.g. steri-strips, glue, adhesives).
Types of outcome measures
Rates of overall wound infection (including superficial, deep or space infections) (30 postoperative days). We will attempt to use the standard definitions of CDC (Horan 2008). If this is not possible, we will use the definitions given by the trial authors.
Rates of severe wound infection (only deep or space infections) (30 postoperative days).
Length of hospital stay.
Rates of readmission.
Adverse events (e.g. rate of wound dehiscence, allergic reaction to staple or suture material) (30 postoperative days).
Patient satisfaction (e.g. hypertrophic and keloid scarring at maximal 12-month follow-up).
Pain, measured by a validated scale.
Search methods for identification of studies
We will search the following electronic databases to identify reports of relevant randomised clinical trials::
Cochrane Wounds Group Specialised Register;
Cochrane Central Register of Controlled Trials (CENTRAL) (latest issue);
The Database of Abstracts of Reviews of Effects (DARE) (latest issue);
The NHS Economic Evaluation Database (NHS EED) (latest issue);
Ovid MEDLINE (1946 to present);
Ovid MEDLINE (In-Process & Other Non-Indexed Citations, to date);
EMBASE (1974 to present);
CINAHL (1982 to date).
The following search strategy will be used in the Cochrane Central Register of Controlled Trials (CENTRAL):
#1 MeSH descriptor: [Sutures] explode all trees
#2 MeSH descriptor: [Surgical Staplers] explode all trees
#3 MeSH descriptor: [Surgical Stapling] explode all trees
#4 #2 or #3
#5 #1 and #4
#6 ((sutur* or "hand sewn" or "hand sewing" or stitch* or handsewn or "manual closure" or catgut* or "cat gut") and stapl*):ti,ab
#7 #5 or #6
#8 MeSH descriptor Surgical Wound Infection explode all trees
#9 MeSH descriptor Surgical Wound Dehiscence explode all trees
#10 (surg* near/5 infect*):ti,ab,kw
#11 (surg* near/5 wound*):ti,ab,kw
#12 (surg* near/5 site*):ti,ab,kw
#13 (surg* near/5 incision*):ti,ab,kw
#14 (surg* near/5 dehisc*):ti,ab,kw
#15 (wound* near/5 dehisc*):ti,ab,kw
#16 (wound* near/5 infect*):ti,ab,kw
#17 (wound near/5 disruption*):ti,ab,kw
#18 (wound next complication*):ti,ab,kw
#19 #8 or #9 or #10 or #11 or #12 or #13 or #14 or #15 or #16 or #17 or #18
#20 #7 and #19
We will search the following in an effort to identify published, unpublished and ongoing trials:
The search strategies for Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL are in found in Appendix 2; Appendix 3 and Appendix 4 respectively.
We will adapt this strategy to search Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL. We will combine the MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity- and precision-maximising version (2008 revision) (Lefebvre 2011). We will combine the EMBASE search with the Ovid EMBASE filter developed by the UK Cochrane Centre (Lefebvre 2011). We will combine the CINAHL searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2011).
We will check the reference lists of all relevant papers, such as systematic reviews or meta-analyses identified through the database searches. There will be no date, language or publication status restrictions.
Searching other resources
In addition, we will search the references of relevant studies. We will contact commercial companies providing sutures and staples (e.g. US Surgical Corporation Autosuture Company, Ethicon, Johnson & Johnson) to ask for references to relevant studies or unpublished data.
Data collection and analysis
Selection of studies
One review author (RC) will run all the electronic searches, download the references into bibliographic software and remove duplicates. Two review authors (RC, AR) will independently assess the titles and abstracts first and then only assess in full text the studies that appear to be relevant. Disagreements will be resolved through discussion with the review team and the arbitrator (AM). One of the review authors (EM) will contact the corresponding author of the publications if data are missing or clarification is needed.
Data extraction and management
We will construct a data extraction sheet for the review and two review authors (RC, GC) will use this independently for data collection. These authors will be blinded to each other's data; however, they will not be blinded to the journal of publication or the trial authors.
Two review authors will independently extract the following information from each included trial:
If information is missing from the published paper, we will contact the trial authors. We will compare results to check for inconsistencies and resolve disagreements by discussion or, if consensus cannot be reached, through adjudication by a third review author (EM).
Assessment of risk of bias in included studies
Two review authors will independently assess the included studies using The Cochrane Collaboration tool for assessing risk of bias (Higgins 2011). This tool addresses six specific domains: sequence generation, allocation concealment, blinding, incomplete data, selective outcome reporting and other issues (Appendix 5). We will assess blinding and completeness of outcome data for each outcome separately. We will complete a 'Risk of bias' table for each eligible study. We will discuss any disagreement amongst all review authors to achieve a consensus.
We will present our assessment of risk of bias using two 'Risk of bias' summary figures; one which is a summary of bias for each item across all studies, and a second which shows a cross-tabulation of each trial by all of the 'Risk of bias' items. This display of internal validity indicates the weight the reader may give the results of each study. For trials using cluster-randomisation, we will assess the risk of bias using the following domains: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis and comparability with individually randomised trials (Higgins 2011).
Measures of treatment effect
We will express the treatment effects as risk ratios (RR) with 95% confidence intervals (CI) for dichotomous outcomes (e.g. rate of infection, rate of readmission).
We will be analyse continuous data (e.g. length of stay, pain) as mean differences (MD) or standardised mean differences (SMD) with standard deviations. We will report time-to-event data (e.g. time to complete wound healing) as hazard ratios (HR) where possible; where these data are incorrectly reported as continuous we will present these results narratively. We will attempt to convert outcome measures into the same metric when possible to ease interpretation and reduce heterogeneity.
Unit of analysis issues
The unit of analysis is the surgical wound subject to the type of skin closure. While we will accept the results from studies in which multiple incisions were randomised to different treatment groups, we will not analyse studies in which a part of the surgical incision is randomised to one group and the rest of the incision to another group.
Dealing with missing data
In the case of missing data, we will contact the study authors. When possible, we will perform intention-to-treat analyses including all participants according to their original allocation. Where binary data are missing, we will perform a worst-case scenario analysis of the main outcome. Such analysis in this case will assume that those patients who were lost to follow-up in the treatment group had the worse outcome, while patients lost to follow-up in the control group had the best outcome. We will compare the effects of the primary analysis with the worst-case analysis to explore whether they have the same direction and magnitude. Where continuous data are missing, we will impute the missing values with replacement data when possible. We will conduct a sensitivity analysis comparing the results with and without imputation. We will impute no more than 10% of the data.
Assessment of heterogeneity
We will assess heterogeneity both by a visual inspection of the forest plot (overlapping of horizontal lines) and through examination of the Chi2 test and I2 statistic. We will consider outcomes with a statistically significant Chi2 value at the 0.10 level and I2 values greater than 50% to be statistically heterogeneous. In the case of statistical heterogeneity, we will then ensure that the data and effect sizes are correct. If they are, we will attempt to explore heterogeneity through an analysis of the subgroups mentioned below. If there is extreme heterogeneity (e.g. if I2 values are over 75% or if there is inconsistent direction of the effects), we will not perform pooling. If there are studies that appear to be outliers, we will conduct an analysis with and without the outliers. If heterogeneity cannot be sufficiently explained, we will account for the heterogeneity by using a random-effects model.
Assessment of reporting biases
If there are 10 or more studies included for a particular outcome we will produce a funnel plot using RevMan (RevMan 2014), with the aim of looking for signs of asymmetry with respect to reporting bias.
Two review authors will independently extract data from the included trials. We will summarise the main characteristics and results of the included studies. In terms of data synthesis, we plan to use a fixed-effect model for non-statistically heterogeneous outcomes. We will use a random-effects model for statistically heterogeneous outcomes in which the heterogeneity cannot be explained through a subgroup analysis. In the case of rare events (defined here as risks of 1 in 100 or less), we will use the Peto one-step odds ratio method. An exception to using the Peto method for rare events will occur when the risk ratio is less than 0.02 or greater than 5.00 or when the event risk is about 1% and when the N size is two or more times greater in one condition than the other. In that case, we will also report logistic regression results (Bradburn 2007).
To summarise the methods and results we will include a PRISMA (preferred reporting items for systematic reviews and meta-analyses) study selection flow chart (Liberati 2009), a 'Characteristics of included studies' table and forest plots for each synthesised outcome and other tables and figures as appropriate. In terms of interpretation, we will use the GRADE approach to assess the quality of the evidence and provide "clarification of the manner in which particular values and preferences may bear on the balance of benefits, harms, burden and costs of the intervention" (Higgins 2011; Schünemann 2011). In the discussion section, we will use the five subheadings suggested in the Cochrane Handbook for Systematic Reviews of Interventions (risk of bias, indirectness, inconsistency, imprecision and publication bias). We plan to create a 'Summary of findings' table that will include all the primary outcomes mentioned above.
Subgroup analysis and investigation of heterogeneity
We will conduct subgroup analyses in relation to the type of surgery (e.g. thoracic surgery, upper digestive surgery, neck surgery, breast surgery, colorectal surgery, obstetric surgery) and who conducted the closure.
To investigate heterogeneity we will use Borenstein's method for investigating heterogeneity across subgroups (Borenstein 2008). We will also examine the I2 statistic across subgroups.
We will perform sensitivity analyses to explore the effect of the following methodological characteristics:
Allocation concealment: we will re-analyse the data excluding trials at unclear or high risk of bias for allocation concealment.
Random-effects versus fixed-effect models: we will re-analyse the data using both random-effects and fixed-effect models to see if there are substantive differences in interpretation.