Subcuticular sutures for skin closure in non‐obstetric surgery

Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To examine the efficacy and acceptability of subcuticular sutures for skin closure in non‐obstetric surgery.

Background

Description of the condition

Many people undergo surgical procedures in their lifetime. It is estimated that 312.9 million operations are undertaken every year worldwide (95% confidence interval (CI) 266.2 to 359.5; Weiser 2015). Since Weiser 2015 reports that 18.7 million of these are caesarean deliveries, we can estimate that approximately 250 to 300 million of them are non‐obstetric surgeries. In most operations, surgeons make an incision to gain access to the tissue or organs in which the surgery is performed. After the surgical procedure is complete, they close the incision with various wound closure materials (e.g. sutures, tissue adhesives, surgical tapes, staples) and suturing techniques (Regula 2015; Tajirian 2010).

Wound complications such as surgical site infections (SSI) are among the most common issues reported after surgery, and are often very problematic for patients in terms of cosmetic appearance, decreased quality of life, prolonged hospital stays, and increased healthcare costs (de Lissovoy 2009; Perencevich 2003; Zimlichman 2013).

Incidence of wound complications depends on various risk factors including those related to patients (e.g. comorbidities, medications), those related to operations (e.g. the type of surgery, duration of operation and method of wound closure), and preventive measures (Cardo 2004; Gaynes 2001; Kwon 2013; Mangram 1999; Pull ter Gunne 2012; Talbot 2005; Zhang 2014; Zhang 2015).

In the USA, the Centers for Disease Control and Prevention (CDC) provide guidelines and tools for the healthcare community to help prevent SSI, together with resources to help the public understand these infections and take measures to safeguard their own health when possible. Many preventive measures against SSI are recommended and have spread globally. The incidence of SSI varies and depends on the classification of surgical wounds (Garner 1986). The Garner 1986 guideline categorises operative wound sites into four classes (classes 1 to 4) according to the degree of contamination, that is: clean (class 1), clean‐contaminated (class 2), contaminated (class 3), and dirty or infected (class 4) (Garner 1986). This classification is shown in more detail in Appendix 1. CDC recommend taking different preventive approaches according to each class (Mangram 1999).

Description of the intervention

There are many ways to close surgical incisions, for example, using sutures, staples, and other devices (e.g. tissue adhesives, tapes) (Dumville 2014; Regula 2015; Tajirian 2010). Conventional sutures are usually non‐absorbable interrupted sutures (individual stitches, typically placed transdermally) (Pauniaho 2010). Staples are usually non‐absorbable skin closure clips placed transdermally. Other devices for wound closure include tissue adhesives or tapes, but their use is less widespread due to problems with wound dehiscence (breakdown) (Dumville 2014). In addition, costs are increased because of the high price of adhesive compared to that for subcuticular and other sutures. Brown 2009 reported that, for closure of pediatric hernia incisions, material costs related to skin closure were higher for skin adhesive than for suturing (suture materials USD 11.70 versus skin adhesive USD 22.63; P value < 0.001).

Subcuticular suturing was introduced by Carl Thiersch in 1874. The development of the subcuticular suture sprang from concepts for improving wound healing and avoiding infection (Fisher 1980). Subcuticular suturing became known in the field of plastic surgery in the early 1900s through the efforts of Dr Halsted and Dr Davis (Fisher 1980). 'Subcuticular' means intradermal; i.e. within the layer of the skin (immediately below the epidermal layer). Subcuticular sutures can be either absorbable or non‐absorbable . When non‐absorbable filaments are used, the suture ends are not buried in the skin but exposed outside, which can increase the risk of contamination (Stanec 1997). On the other hand, when absorbable sutures are used, they can be completely buried and retained at or near wound ends (La Paudula 1995; Ranaboldo 1992; Singh‐Ranger 2003; Smoot 1998). Synthetic absorbable filaments (e.g. polyglecaprone, polydioxanone, polyglactin) have only recently become available and are now used widely. Prior to this only natural absorbable filaments (e.g. catgut) were available, but they were rarely used for skin closure due to the risk of infection. With subcuticular sutures, no foreign material reaches beyond the epidermis except for the suture ends. This does not leave any mark points (Kobayashi 2015).

Subcuticular sutures were not previously the preferred method of skin closure except for in clean surgery, because of the risk of infection. Since the arrival of synthetic absorbable sutures, their use has been spreading rapidly, not only for CDC class 1 (clean) surgery, but also for class 2 and 3 procedures, partly because wound cosmesis is currently considered more important than it was previously (Tanaka 2014; Taube 1983). The recent development of suture filaments and surgical devices, and the fact that endoscopic surgery is now more widely performed also lie behind the trend.

How the intervention might work

The use of subcuticular sutures for skin closure is an attractive alternative closure method because of the low incidence of wound complications and good cosmetic appearance it produces (Fisher 1980). With subcuticular sutures, no foreign material reaches beyond the epidermis except for the suture ends. This can obviate the need for postoperative suture removal except for the suture ends and does not leave any mark points (Kobayashi 2015).

Common alternatives to subcuticular sutures are conventional transdermal sutures and staples, both of which have to be removed. Staples are attractive because of speed of application (Gatt 1985; Tajirian 2010), however their cost is higher than that of suture filaments in general.

Compared with staples or conventional transdermal sutures, some clinical trials have shown that subcuticular sutures are associated with a lower incidence of wound complications and better cosmetic results after CDC class 1 (clean) surgery such as: orthopaedic procedures (Shetty 2004), cardiovascular surgery (Angelini 1984; Johnson 1997), and obstetric surgery (Ibrahim 2014; Mackeen 2012; Mackeen 2015). For closure of hip wounds, a cost‐effectiveness study showed that subcuticular sutures were significantly better than clips in terms of wound healing and also in terms of cost (Singh 2006). It has also been reported that the cost incurred for closure of sternal and leg incisions in coronary arterial bypass grafting (CABG) patients was significantly greater when skin clips were used for closure than when sutures were used (Angelini 1984; Chughtai 2000; Johnson 1997). Chughtai 2000 reported a cost of USD 4.5 for each wound closed with sutures and USD 15 for each wound closed with staples. In CDC class 2 (clean‐contaminated) surgery such as gastrointestinal procedures, several randomised controlled trials have shown that subcuticular sutures do not increase the incidence of wound complications (Tsujinaga 2013), and that patients prefer this closure technique because it produces better cosmetic results and less pain (Tanaka 2014).

The advantage of subcuticular sutures may be partly attributable to the use of absorbable sutures (Gurusamy 2014); the advantage of absorbable suture materials is that they do not have to be removed later, which saves surgeons time and decreases the anxiety and discomfort of patients (Parell 2003).

Absorbable sutures may, however, lead to an increased inflammatory response (Parell 2003), and it should be noted that the cost of absorbable suture filaments is higher than that for non‐absorbable filaments.

Why it is important to do this review

Two systematic reviews and two meta‐analyses that evaluated subcuticular sutures in cesarean deliveries have been published. One systematic review did not find conclusive evidence about how the skin should be closed (Mackeen 2012), but the others concluded that there was a possible benefit with subcuticular sutures compared to skin staples, because of a lower incidence of wound complications (Clay 2011; Mackeen 2015; Tuuli 2011).

In the field of non‐obstetric surgery, however, there is still controversy about whether subcuticular sutures increase the incidence of wound complications, and, to date, no systematic review has been conducted on this important topic.

One related systematic review entitled 'Continuous versus interrupted skin sutures for non‐obstetric surgery' showed that superficial wound dehiscence may be reduced by using continuous subcuticular sutures (Gurusamy 2014). The authors suggested that this difference might depend on whether sutures were absorbable or not, because most of these wound dehiscences were reported in two recent trials in which the continuous skin suture groups received absorbable subcuticular sutures, while the interrupted skin suture groups received non‐absorbable transcutaneous sutures. In this review, we will focus on investigating the advantages of subcuticular sutures regardless of whether they are continuous or interrupted.

Objectives

To examine the efficacy and acceptability of subcuticular sutures for skin closure in non‐obstetric surgery.

Methods

Criteria for considering studies for this review

Types of studies

We will include all relevant published and unpublished RCTs that compared subcuticular sutures with any other sutures or devices for skin closure in non‐obstetric surgery, irrespective of their sample sizes and language of report.

We will include cluster‐randomised trials when effects of clustering are taken into account. We will exclude quasi‐randomised controlled trials (in which treatment assignment is decided through methods such as alternate days of the week). No language or publication status restrictions will be imposed.

Types of participants

We will include patients of any age and sex undergoing non‐obstetric surgery. We will include both outpatients and inpatients with any type of disease and with any comorbidities.

We will exclude obstetric operations because there is already a Cochrane Review that addresses methods of skin closure after caesarean sections (Mackeen 2012).

Types of interventions

Subcuticular sutures versus any other sutures or devices for skin closure in non‐obstetric surgery

Experimental interventions

We will include studies that used absorbable and non‐absorbable subcuticular sutures for skin closure, irrespective of whether the sutures were continuous or interrupted.

Comparator interventions

We will include studies in which a conventional suture (e.g. transdermal interrupted suture) or a device for skin closure (e.g. staples and other skin closure devices) was used as a control intervention.

Types of outcome measures

Primary outcomes

• Incidence of surgical site infection (SSI) within 30 days of the operation

Secondary outcomes

• Incidence of wound complications (e.g. haematoma, seroma, skin separation) within 30 days of the operation.

When the data allow, we will also present the results for specific outcome subcategories, such as complications of higher severity or specific type.

• Proportion of reclosure of the skin incision required within 60 days of the operation.

• Incidence of hypertrophic scar at maximal follow‐up.

• Incidence of keloid scar at maximal follow‐up.

• Wound pain intensity within seven days, and at or after 30 days of the operation (as measured on visual analogue scale, numerical rating scale or other valid instruments).

• Length of hospital stay (for inpatient surgery, includes any readmissions for wound‐related complications as defined by the authors for a period of one year).

• Cosmesis of scar (as defined by the authors for a minimum follow‐up of six months).

• Patient satisfaction as defined by the authors within 30 days, and at or after 60 days of the operation.

• Quality of Life (QoL; short‐term and long‐term as defined by the authors).

• Wound closure time in the operation (minutes).

• Cost at maximal follow‐up (as reported by authors).

Search methods for identification of studies

Electronic searches

We will search the following electronic databases to identify reports of relevant randomised clinical trials:

• The Cochrane Wounds Specialised Register (to present);

• The Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library) (latest issue);

• Ovid MEDLINE (1946 to present);

• Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations) (latest issue);

• Ovid EMBASE (1974 to present);

• EBSCO CINAHL Plus (1937 to present).

A provisional search strategy for the Cochrane Central Register of Controlled Trials (CENTRAL) can be found in Appendix 2. We will adapt this strategy to search Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL. We will combine the Ovid 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 search with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2014). We will not restrict studies with respect to language, date of publication or study setting.

We will search the following clinical trials registries:

• ClinicalTrials.gov (www.clinicaltrials.gov/);

• WHO International Clinical Trials Registry Platform (ICTRP) (http://apps.who.int/trialsearch/Default.aspx);

• EU Clinical Trials Register Platform (https://www.clinicaltrialsregister.eu/);

• University hospital Medical Information Network Clinical Trials Registry (UMIN‐CTR) (www.umin.ac.jp/ctr/index‐j.htm).

Searching other resources

We will search the bibliographies of all retrieved and relevant publications identified by these strategies for further studies. We will check the reference lists of all included studies and relevant systematic reviews to identify additional studies missed from the original electronic searches.

A citation search will also be conducted on the Web of Science to identify articles that cite any of the included studies.

We will identify and contact experts and industry representatives to enquire about unpublished or ongoing studies. We intend to contact suture manufactures, such as Ethicon and Covidien.

Data collection and analysis

Selection of studies

Two review authors (SG and KH) will examine the titles and abstracts of references identified by the electronic search strategies described above to determine which are likely to be relevant. We will obtain the full text for each potentially relevant study. These two authors will assess each article independently, and decide whether to include the study in the meta‐analysis. Disagreement between authors will be resolved by discussion. If necessary, arbitration will be provided by a third author (TAF). Agreement between review authors in the study selection will be reported. The disagreement in the selection of studies will be evaluated by quantifying both the percentage of agreement and Cohen's kappa (k) (Cohen 1960).

When missing information inhibits the evaluation of a study, we will classify the study as a 'Study awaiting assessment' and seek further information from the original authors or other possible sources. We will describe the reasons for exclusion of studies in the 'Characteristics of excluded studies' table. The study selection process will be reported in a PRISMA flow diagram to summarise this process (Liberati 2009).

Data extraction and management

Independently, two review authors (SG and KH) will extract information from the included trials using a structured, pilot‐tested, Excel data extraction form. Any disagreement will be resolved either by discussion or by consultation with a third author (TAF). If necessary, authors of studies will be contacted to obtain further clarification. Agreement between the data extractors will be reported.

This data extraction form includes the following items.

• General information: title, authors, and year of publication of the first report.

• Study characteristics including design, setting, country, and duration of the study.

• Participants: total number; number of each age, sex, and comorbidity; type of surgery; and wound class.

• Interventions and comparisons: total number of intervention groups, type of interventions, and type of suture materials and suturing method in each arm.

• Outcomes: definition of outcomes, number of participants allocated to each intervention group, sample size, number of missing participants, number of events (dichotomous outcomes), standard deviation (SD) and mean (continuous outcomes), timing of assessment, and duration of follow‐up.

• Risk of bias and publication status.

Assessment of risk of bias in included studies

Independently, two review authors (SG and HK) will assess the risk of bias of the included studies using the criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). If assessors disagree, the final rating will be made by discussion or with the involvement of a third assessor (TAF), if necessary. Agreement between the two independent raters in the 'Risk of bias' assessment will be reported as percentage agreement and weighted kappa. The following domains will be assessed (see Appendix 3):

• random sequence generation;

• allocation concealment;

• blinding of participants and personnel;

• blinding of outcome assessment;

• incomplete outcome data;

• selective outcome reporting;

• other bias (distribution of baseline characteristics, industry funding etc.).

The risk of bias in each domain will be assessed and categorised into:

• low risk of bias, i.e. plausible bias that is unlikely to alter the results seriously;

• high risk of bias, i.e. plausible bias that seriously weakens confidence in the results;

• unclear risk of bias, i.e. plausible bias that raises some doubt about the results.

Where inadequate details of randomisation and other characteristics of trials are provided, the risk of bias will be classified as unclear, unless further information can be obtained by contacting the authors. We will provide a quote from the study report together with a justification for our judgment in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgments across different studies for each of the domains listed. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

Measures of treatment effect

We will use Review Manager 5.3 to analyse the data. We expect to identify both dichotomous data and continuous data.

Dichotomous data

For binary outcomes, we will present results as the risk ratio (RR) with 95% CI, because risk is a concept that is more familiar and simple to clinicians than odds.

Continuous data

Wherever possible we will express continuous data as mean difference (MD) with 95% CI. In cases where different scales are used to measure the same or similar construct, we will use the standardised mean difference (SMD) with 95% CI for continuous outcomes.

Endpoint versus change data

We will use endpoint data, which typically cannot have negative values and are easier to interpret from the clinical point of view. If endpoint data are not available, we will use the change data. We consider this strategy to be less prone to selective reporting.

Time‐to‐event data

For time‐to‐event data our primary effect measure will be the hazard ratio (HR) with 95% CI.

Skewed data

To avoid analysing skewed data as normally distributed data, we will apply the following standards to all data before inclusion.

• We will enter data from studies of at least 100 participants into the analysis irrespective of the following rules, because skewed data pose less of a problem in large studies.

• Endpoint data: when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean and divide this by the standard deviation.

  • If this value is lower than 1.0, it strongly suggests a skew and we will exclude the study from meta‐analytic pooling and present it narratively.

  • If this ratio is higher than 1.0 but below 2.0, there is suggestion of a skew. We will enter the study in the analysis and test whether its inclusion or exclusion changes the results substantially.

  • If the ratio is larger than 2.0, the study will be included in the analysis because skew is less likely (Altman 1996; Higgins 2011).

• When continuous data are presented on a scale that includes the possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will enter such studies into the analysis because change data tend to be less skewed than other data and because excluding studies will also lead to bias, as not all the available information would be used.

• A common way that trialists indicate that they have skewed data is by reporting medians and interquartile ranges. When we encounter this, we will note that the data are skewed and the study will be excluded from meta‐analytic pooling and will be summarised narratively.

Unit of analysis issues

Cluster‐randomised trials

In cluster‐randomised trials, groups of individuals rather than individuals are randomised to different interventions (Higgins 2011). Cluster‐randomised trials will only be included when effects of clustering are taken into account.

When cluster‐randomised trials are analysed as if the randomisation was performed on the individuals rather than the clusters, we will perform approximately correct analyses. The idea is to reduce the size of each trial to its 'effective sample size' (Rao 1992). The effective sample size of a single intervention group in a cluster‐randomised trial is its original sample size divided by a quantity called the 'design effect'. The design effect calculated by the equation: 1 + (M – 1) ICC, where M is the average cluster size and ICC is the intra cluster correlation coefficient. A common design effect is usually assumed across intervention groups. For dichotomous data, both the number of participants and the number experiencing the event will be divided by the same design effect. For continuous data, only the sample size will be reduced; means and standard deviations should remain unchanged.

Multiple body parts Ⅰ: body parts receive the same intervention

In some studies where people are randomised and multiple incisions of the body receive the same intervention, a separate outcome judgement is made for each incision, and the number of incisions is used as the denominator in the analysis. This is similar to the situation in cluster‐randomised trials, except that participants are the 'clusters'.

Multiple body parts Ⅱ: body parts receive different interventions

If multiple incisions are randomised to different groups, we plan to include the trial only if appropriate analysis is undertaken to take within‐subject correlation into account, or if it is possible to perform such an analysis using the available data.

While we plan to accept the results from trials in which multiple incisions are randomised to different intervention groups, we will not accept trials in which a part of the surgical incision was randomised to one intervention and the rest of the incision to another intervention.

These trials have similarities to cross‐over trials: in cross‐over trials individuals receive multiple treatments at different times, while in these trials they receive multiple treatments at different sites.

Dealing with missing data

We will try to contact authors of trials to obtain any missing data.

Missing participants

Dichotomous data

All dichotomous data will be analysed on the basis of the intention‐to‐treat (ITT) principle. When participants have been withdrawn from a trial and the original authors have not imputed it appropriately, we will assume that the condition of these participants would have remained unchanged if they had stayed in the trial, or we will treat them as treatment failures (a 'worst‐case' scenario). We will perform sensitivity analyses to assess how sensitive results are to reasonable changes in the assumptions. We will address the potential impact of missing data on the findings of the review in the Discussion.

Continuous data

We will use continuous data as they are presented by the original authors, without any imputations according to the recommendation in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Whenever ITT data are presented by the authors, they will be preferred to 'per protocol or completer' data sets.

Missing data

We will contact investigators or study sponsors in order to obtain numerical outcome data where possible (e.g. when a study is identified as abstract only).

Missing statistics

When only P values or standard error (SE) values have been reported, we will calculate standard deviations (SDs) (Altman 1996). In the absence of supplemental data after requests to the original authors, we will calculate SDs from CIs, T values, or P values as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Otherwise, we will impute them from other studies in the meta‐analysis according to a validated method developed by Furukawa (Furukawa 2000). We will examine the validity of these imputations in a sensitivity analysis.

Assessment of heterogeneity

Initially, we will investigate heterogeneity by visual inspection of the forest plots. We will perform the Chi² test in order to detect the presence of heterogeneity. We will regard heterogeneity as present if there is a low P value (less than 0.10) in the Chi² test for heterogeneity. Since the Chi² test has low power to assess heterogeneity when a small number of participants or studies are included, we will set the probability at the 10% level of significance. We will also calculate the I² statistic in order to assess the degree of heterogeneity (Higgins 2002). The I² statistic is defined as the proportion of total heterogeneity that exceeds what would be expected due to chance (Higgins 2003). It will be interpreted as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), as follows: 0% to 40% might not be important; 30% to 60% may represent moderate heterogeneity; 50% to 90% may represent substantial heterogeneity; 75% to 100% represents considerable heterogeneity.

We will also report Tau², that is, the between study variance in random‐effects model meta‐analyses.

If apparent or statistical heterogeneity is identified, we will investigate its potential sources through subgroup and sensitivity analyses.

Assessment of reporting biases

We will assess publication bias by a funnel plot if the number of studies included is 10 or more. We will investigate the presence of small study effects for the primary outcome only; along with visual inspection of the plots, we will use Egger's test to examine whether the association between estimated intervention effects and the study size is greater than might be expected to occur by chance (Egger 1997).

Data synthesis

We will perform meta‐analyses according to the recommendations of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will use a random‐effects model in analysis because we consider that the different studies will estimate different, yet related, intervention effects (DerSimonian 1986). We will use a fixed‐effect model for sensitivity analysis.

With regard to dichotomous outcomes, risk ratio calculations do not include trials in which no events occurred in either group in the meta‐analysis, whereas risk difference calculations do. We plan to report the risk difference (RD) if the results using this association measure are different from risk ratio in terms of statistical significance. However, risk ratio is the measure that we plan to use to arrive at conclusions, since risk ratios perform better when there are differences in the control event rate (proportion of participants who develop the event in the control groups) (Furukawa 2002).

Subgroup analysis and investigation of heterogeneity

Subgroup analyses are often exploratory in nature and should be interpreted cautiously. Firstly, because these analyses often involve multiple analyses, they may yield false positive results; secondly, these analyses lack power and are more likely to result in false negative results. With these reservations in mind, we will perform the following subgroup analysis for the primary outcome only.

We plan to conduct the following a priori subgroup analyses:

• absorbable versus non‐absorbable subcuticular sutures;

• location of surgery on the body (trunk, extremities, and face) as wound healing rates may be different;

• CDC class 1 (clean) versus class 2 (clean‐contaminated) versus class 3 (contaminated) surgery;

• continuous versus interrupted skin sutures;

• endoscopic (e.g. laparoscopic, thoracoscopic and arthroscopic) versus open surgery.

Sensitivity analysis

The process of undertaking a systematic review and meta‐analyses involves a sequence of decisions that may be somewhat arbitrary or unclear (Higgins 2011). A sensitivity analysis is a repeat of the primary analysis in which alternative decisions or ranges of values are substituted for decisions that were arbitrary or unclear. We plan to perform the following sensitivity analyses for the primary outcome only.

• Restrict inclusion in the analysis to only those studies that are considered to be at a low risk of selection bias (i.e. adequate allocation sequence generation and adequate allocation concealment). Since it will be impossible for both the operators of the procedure and assessors of outcomes to be blinded to the intervention, we will not use blinding of personnel and outcome assessment as a marker of trial quality.

• Examine handling of missing participants firstly by ITT analysis based on the worst case scenario, and secondly by per protocol analysis.

• Exclude studies sponsored by companies that produce suture devices, as they have an inevitable conflict of interest.

• For meta‐analyses, use a fixed‐effect model instead of a random‐effects model.

'Summary of findings' tables

We will present the main results of the review in 'Summary of findings' tables, which will provide key information concerning the quality of evidence, the magnitude of the effect of the interventions examined, and the sum of the available data on the main outcomes, as recommended by Cochrane (Schünemann 2011a). The 'Summary of findings' tables will also include an overall grading of the body of evidence related to each of the main outcomes using the GRADE (Grading of Recommendations Assessment, Development and Evaluation) approach (Schünemann 2011b).

We have selected seven outcomes as the most clinically relevant outcomes.

We will present 'Summary of findings' tables for the primary outcome and the following six secondary outcomes:

• incidence of wound complications (e.g. haematoma, seroma, skin separation) within 30 days of the operation;

• cosmesis of scar (as defined by the authors for a minimum follow‐up of six months);

• patient satisfaction (as defined by the authors, within 30 days, and at, or after, 60 days of the operation);

• Quality of Life (QoL) (short‐term and long‐term as defined by the authors);

• wound closure time in the operation (minutes);

• cost at maximal follow‐up (as reported by authors).

Appendices

Appendix 1. Classification of surgical wound

Class 1: clean	An uninfected operative wound in which no inflammation is encountered and the respiratory, alimentary, genital, or uninfected urinary tract is not entered. In addition, clean wounds are primarily closed and, if necessary, drained with closed drainage. Operative incisional wounds that follow nonpenetrating (blunt) trauma should be included in this category if they meet the criteria.
Class 2: clean‐contaminated	An operative wound in which the respiratory, alimentary, genital, or urinary tracts are entered under controlled conditions and without unusual contamination. Specifically, operations involving the biliary tract, appendix, vagina, and oropharynx are included in this category, provided no evidence of infection or major break in technique is encountered.
Class 3: contaminated	Open, fresh, accidental wounds. In addition, operations with major breaks in sterile technique (e.g. open cardiac massage) or gross spillage from the gastrointestinal tract, and incisions in which acute, nonpurulent inflammation is encountered are included in this category.
Class 4: dirty‐infected	Old traumatic wounds with retained devitalised tissue and those that involve existing clinical infection or perforated viscera. This definition suggests that the organisms causing postoperative infection were present in the operative field before the operation.

Appendix 2. The Cochrane Central Register of Controlled Trials (CENTRAL) provisional search strategy

#1 MeSH descriptor: [Subcutaneous Tissue] explode all trees

#2 hypoderm* or subderm* or intraderm*:ti,ab,kw (Word variations have been searched)

#3 (subcutaneous or sub‐cutaneous or subcuticular or sub‐cuticular):ti,ab,kw

#4 (buried):ti,ab,kw

#5 {or #1‐#4} in Trials

#6 MeSH descriptor: [Sutures] explode all trees

#7 MeSH descriptor: [Wound Closure Techniques] explode all trees

#8 (sutur* or stitch* or closure or close or closing*):ti,ab,kw

#9 (Monocryl or Vicryl or PDS):ti,ab,kw

#10 {or #6‐#9} in Trials

#11 #5 and #10

Appendix 3. Criteria for judging risk of bias in the 'Risk of bias' assessment tool

RANDOM SEQUENCE GENERATION Selection bias (biased allocation to interventions) due to inadequate generation of a randomised sequence
Criteria for a judgement of low risk of bias	The investigators describe a random component in the sequence generation process such as: referring to a random number table; using a computer random number generator; coin tossing; shuffling cards or envelopes; throwing dice; drawing of lots; minimisation*. *Minimisation may be implemented without a random element, and this is considered to be equivalent to being random.
Criteria for a judgement of high risk of bias	The investigators describe a non‐random component in the sequence generation process. Usually, the description would involve some systematic, non‐random approach, for example generating the sequence: by odd or even date of birth; by some rule based on date (or day) of admission; by some rule based on hospital or clinic record number. Other non‐random approaches happen much less frequently than the systematic approaches mentioned above and tend to be obvious. They usually involve judgement or some method of non‐random categorisation of participants, for example allocation: by clinician's judgement; participant's preference; based on the results of a laboratory test or a series of tests; by availability of the intervention.
Criteria for a judgement of unclear risk of bias	Insufficient information about the sequence generation process is available to permit a judgement of 'low risk' or 'high risk'.
ALLOCATION CONCEALMENT Selection bias (biased allocation to interventions) due to inadequate concealment of allocations prior to assignment
Criteria for a judgement of low risk of bias	Participants and investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.
Criteria for a judgement of high risk of bias	Participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias, such as allocation based on: using an open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards (e.g. if envelopes were unsealed or non­opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure.
Criteria for a judgement of unclear risk of bias	Insufficient information available to permit a judgement of 'low risk' or 'high risk'. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement – for example if the use of assignment envelopes is described, but it remains unclear whether envelopes were sequentially numbered, opaque and sealed.
BLINDING OF PARTICIPANTS AND PERSONNEL Performance bias due to knowledge of the allocated interventions by participants and personnel during the study
Criteria for a judgement of low risk of bias	Either of the following: no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding; blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken.
Criteria for a judgement of high risk of bias	Either of the following: no blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding; blinding of key study participants and personnel attempted, but likely that the blinding could have been broken, and the outcome is likely to be influenced by lack of blinding.
Criteria for a judgement of unclear risk of bias	Either of the following: insufficient information available to permit a judgement of 'low risk' or 'high risk'; the study did not address this outcome.
BLINDING OF OUTCOME ASSESSMENT Detection bias due to knowledge of the allocated interventions by outcome assessors
Criteria for a judgement of low risk of bias	Either of the following: no blinding of outcome assessment, but the review authors judge that the outcome measurement is not likely to be influenced by lack of blinding; blinding of outcome assessment ensured, and unlikely that the blinding could have been broken.
Criteria for a judgement of high risk of bias	Either of the following: no blinding of outcome assessment, and the outcome measurement is likely to be influenced by lack of blinding; blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement is likely to be influenced by lack of blinding.
Criteria for a judgement of unclear risk of bias	Either of the following: insufficient information available to permit a judgement of 'low risk' or 'high risk'; the study did not address this outcome.
INCOMPLETE OUTCOME DATA Attrition bias due to amount, nature or handling of incomplete outcome data
Criteria for a judgement of low risk of bias	Any one of the following: no missing outcome data; reasons for missing outcome data are unlikely to be related to true outcome (for survival data, censoring is unlikely to introduce bias); missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; for dichotomous outcome data, the proportion of missing outcomes compared with the observed event risk is not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, the plausible effect size (difference in means or standardised difference in means) among missing outcomes is not enough to have a clinically relevant impact on observed effect size; missing data have been imputed using appropriate methods.
Criteria for a judgement of high risk of bias	Any one of the following: reason for missing outcome data is likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; for dichotomous outcome data, the proportion of missing outcomes compared with the observed event risk is enough to induce clinically relevant bias in the intervention effect estimate; for continuous outcome data, the plausible effect size (difference in means or standardised difference in means) among missing outcomes is enough to induce clinically relevant bias in the observed effect size; 'as‐treated' analysis done with substantial departure of the intervention received from that assigned at randomisation; potentially inappropriate application of simple imputation.
Criteria for a judgement of unclear risk of bias	Either of the following: insufficient reporting of attrition/exclusions to permit a judgement of 'low risk' or 'high risk' (e.g. number randomised not stated, and no reasons for missing data provided); the study did not address this outcome.
SELECTIVE REPORTING Reporting bias due to selective outcome reporting
Criteria for a judgement of low risk of bias	Either of the following: the study protocol is available and all of the study's prespecified (primary and secondary) outcomes that are of interest in the review have been reported in the prespecified way; the study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were prespecified (convincing text of this nature may be uncommon).
Criteria for a judgement of high risk of bias	Any one of the following: not all of the study's prespecified primary outcomes have been reported; one or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales or subgroups) that were not prespecified; one or more reported primary outcomes were not prespecified (unless clear justification for their reporting is provided, such as an unexpected adverse effect); one or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis; the study report fails to include results for a key outcome that would be expected to have been reported for such a study.
Criteria for a judgement of unclear risk of bias	Insufficient information available to permit a judgement of 'low risk' or 'high risk'. It is likely that the majority of studies will fall into this category.
OTHER BIAS Bias due to problems not covered elsewhere in this table
Criteria for a judgement of low risk of bias	The study appears to be free of other sources of bias.
Criteria for a judgement of high risk of bias	There is at least one important risk of bias. For example, the study: has extreme baseline imbalance; or had a potential source of bias related to the specific study design used; had an inappropriate influence of funders due to industry‐initiated protocols; has been claimed to have been fraudulent; or had some other problem. Or in cluster‐randomised trials there is: recruitment bias (differential participant recruitment in clusters for different interventions); baseline imbalance; loss of clusters; incorrect analysis; comparability with individually randomised trials.
Criteria for a judgement of unclear risk of bias	There may be a risk of bias, but there is either: insufficient information to assess whether an important risk of bias exists; or insufficient rationale or evidence that an identified problem will introduce bias.

What's new

Date	Event	Description
12 July 2019	Amended	Amendment to 'Declarations of interest' section

Contributions of authors

Saori Goto (SG) conceived the idea for this review. SG and Koya Hida (KH) drafted this protocol, Toshi A Furukawa (TAF) commented on all methodological content and approved the final version prior to submission. Yoshiharu Sakai (YS) commented on all surgical content, approved the final version prior to submission, secured funding and is guarantor of the protocol.

Contributions of the editorial base

Kurinchi Gurusamy (Editor): edited the protocol; advised on methodology, interpretation and protocol content; approved the final protocol prior to submission.

Gill Rizzello (Managing Editor): co‐ordinated the editorial process; advised on content; edited the protocol.

Reetu Child (Information Specialist) : designed the search strategy and edited the search methods section.

Sources of support

Internal sources

• No sources of support supplied

External sources

• This project was supported by the National Institute for Health Research via Cochrane Infrastructure funding to Cochrane Wounds. The views and opinions expressed herein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS or the Department of Health, UK.

Declarations of interest

SG declares no competing interests.

KH has a received grants for research (into the treatment of rectal cancer) from the Japanese Society of Clinical Oncology, The Japanese Foundation for Research and Promotion of Endoscopy, and the Fujiwara Memorial Foundation.

TAF has received lecture fees from Eli Lilly, Meiji, Mochida, MSD, Otsuka, Pfizer and Tanabe‐Mitsubishi, and consultancy fees from Sekisui Chemicals and the Takeda Science Foundation. He has received royalties from Igaku‐Shoin, Seiwa‐Shoten and Nihon Bunka Kagaku‐sha publishers. He has received grants or research support from the Japanese Ministry of Education, Science and Technology, the Japanese Ministry of Health, Labour and Welfare, the Japan Society for the Promotion of Science, the Japan Foundation for Neuroscience and Mental Health, Mochida, and Tanabe‐Mitsubishi. He is a diplomate of the Academy of Cognitive Therapy.

YS has received lecture fees from Olympus, Johnson & Johnson, Covidien Japan, Stryker Japan, Chugai, Taiho, Yakult, Takeda, Tsumura and Terumo. He has received grants or research support from Tsumura, Daiichi Sankyo, Chugai, Taiho, Yakult, Shionogi, Otsuka, and Sanofi.

Editorial base comment: this protocol is not compliant with Cochrane's current Commercial Sponsorship policy. The full review is expected to be published within the next 12 months, at which point the majority of review authors and the lead author will be free of conflicts of interest.

Edited (no change to conclusions)