Negative pressure wound therapy for managing the open abdomen in non‐trauma patients

Objectives

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

To assess the effects of NPWT on primary fascial closure for managing the open abdomen in non‐trauma patients in any care setting.

Background

Description of the condition

About 143 million surgical procedures are performed worldwide each year to save lives and prevent disability (Meara 2015). Although the exact number of abdominal operations performed annually worldwide is unknown, about 2,150,000 abdominal operations are performed each year in the UK, 6,100,000 in the USA, 478,000 in Japan, and 1,000,000 in France (Carney 2017; Fingerhut 1998; Miyata 2018). After these operations, a portion of patients' abdominal walls may be left open because of the risk of intra‐abdominal hypertension (Cirocchi 2013; Fitzpatrick 2017; Friese 2012).

Leaving the abdomen open allows the abdominal contents to expand in order to reduce intra‐abdominal pressure and related complications (Beckman 2016; Fitzpatrick 2017). Although the reasons for open abdomen vary in different geographical regions, the two most common indications are management of severe peritonitis (abdominal infection) and damage control surgery (a form of surgery typically performed by trauma surgeons in case of severe unstable injuries) for abdominal trauma (Atema 2015; Coccolini 2017a; Fernández 2016; Hofmann 2017; Sartelli 2015). People with open abdomen are often critically ill and require treatment in the intensive care unit (Acosta 2017; Beckman 2016). Management of the open abdomen is a considerable burden for patients and healthcare professionals and is associated with high mortality (Acosta 2017; Beckman 2016; Hofmann 2017; Seternes 2017). The reported mortality rate ranges from 21% to 55% in different studies (Acosta 2017; Fortelny 2014; Hofmann 2017; Rausei 2018). The main cause of death in these patients is multiple organ dysfunction syndrome (Boele van Hensbroek 2016; Mayr 2006). Open abdomen may also be associated with serious complications, such as severe fluid and heat loss, bowel fistulae formation (an opening connecting the bowel to the body surface or to another hollow organ), loss of abdominal wall domain, and development of incisional hernia (the abnormal exit of tissue or an organ through the wall of the cavity caused by an incompletely healed surgical wound) (Beckman 2016; Chiara 2016; Demetriades 2014). The best way to prevent or reduce these complications is to close the abdomen as soon as possible (Chiara 2016; Cristaudo 2017a; Demetriades 2014; Hofmann 2017). If abdominal closure is not possible, one of the effective methods is to close the abdominal wall temporarily (Chiara 2016; Cristaudo 2017a; Demetriades 2014). The ideal method of temporary abdominal closure should protect abdominal contents, prevent further contamination and intra‐abdominal hypertension, remove any infected fluid, limit infection, make reoperation easy, preserve abdominal wall tissue, avoid fascial edge retraction, help nursing care, facilitate successful abdominal closure, and be inexpensive and cost effective (Chiara 2016; Cristaudo 2017b; Demetriades 2014; Kreis 2013; Rogers 2018).

Description of the intervention

Various temporary abdominal closure techniques have been suggested for managing the open abdomen, such as the Bogota bag (a sterilised intravenous fluid bag sutured to the fascia to allow the abdominal contents to expand), the Wittmann patch (the use of two opposing sheets sutured to the lateral fascia to allow easy reoperation), sterilised zipper, and synthetic mesh (Chiara 2016; Cuesta 1991; Demetriades 2014; Kreis 2013; Quyn 2012; Wittmann 1993). Each technique has advantages and disadvantages and the ultimate goal is to achieve primary fascial closure (Atema 2015; Cristaudo 2017b; Demetriades 2014; Quyn 2012). In recent years, negative pressure wound therapy (NPWT) has been introduced as an alternative for the treatment of critically ill people with open abdomen (Bruhin 2014; Carlson 2013; Demetriades 2014; Hofmann 2017). NPWT is a therapeutic technique using a vacuum dressing and suction pump (negative pressure) to promote wound healing (Chiara 2016; Demetriades 2014; Liu 2018; Dumville 2014; Dumville 2015; Kreis 2013; Rogers 2018; Norman 2020). Several different commercial and non‐commercial products are available for NPWT (Bruhin 2014; Dumville 2014; Dumville 2015; Liu 2018; Norman 2020).The most commonly used NPWT systems are the Barker vacuum pack, the vacuum‐assisted closure (V.A.C., KCI, San Antonio, TX), and the ABThera system (ABThera, KCI, San Antonio, TX) (Demetriades 2014; Fitzpatrick 2017; Montori 2017; Norman 2020). The cost of commercial NPWT systems varies, but is relatively high. For example, each commercial NPWT system (ABThera) costs approximately USD 350 in the USA (Frazee 2013). It is estimated that Medicare payments for NPWT systems increased from USD 24 million to USD 164 million (an increase of almost 583%) in the USA between 2001 and 2007 (HHS 2009).

How the intervention might work

NPWT uses a porous dressing to cover the abdominal contents, with a membrane between the dressing and the abdominal contents (NICE 2013; Norman 2020). Another perforated adhesive membrane is utilised to cover the entire wound and surrounding skin and attached to a suction system with a drainage tube (Liu 2018; Dumville 2014; Dumville 2015; NICE 2013; Norman 2020). The suction system with negative pressure is used to remove fluid and infectious materials from the open abdomen (KCI Medical 2018). NPWT may potentially facilitate wound healing and management of the open abdomen by several different mechanisms. First, the porous dressing may help isolate the abdominal contents from the abdominal wall and external environment. Second, the negative pressure may actively remove fluid, help reduce oedema, and prevent intra‐abdominal hypertension. Third, the pressure effect is thought to promote cellular migration and growth of new blood vessels. Finally, it may provide medial tension, which may help to minimise fascial retraction and facilitate the achievement of primary closure (Liu 2018; Dumville 2014; Dumville 2015; NICE 2013; Norman 2020).

Why it is important to do this review

The use of NPWT for managing the open abdomen is controversial (Atema 2015; Coccolini 2017b; Coccolini 2018; Sartelli 2015). NPWT may potentially benefit patients in terms of reduced mortality and successful primary fascial closure, but it is also possible that it may have no benefits and may be associated with adverse effects, such as increasing the risk of bowel fistulae formation (Carlson 2013; Giudicelli 2017; Hofmann 2017). The National Institute for Health and Clinical Excellence in the UK published guidance about NPWT for the open abdomen in 2013 (NICE 2013). They concluded that evidence was adequate to support the use of NPWT for the open abdomen, but they also encouraged more research on this issue (NICE 2013). One Cochrane Review has assessed the role of NPWT for open traumatic wounds (Iheozor‐Ejiofor 2018). This review is an update of a Cochrane protocol last published in 2016 to assess the role of NPWT for managing the open abdomen for wounds not caused by trauma (Boele van Hensbroek 2016). The aim of our review is to inform decision makers and guide future research.

Objectives

To assess the effects of NPWT on primary fascial closure for managing the open abdomen in non‐trauma patients in any care setting.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs), including cluster RCTs. We will include studies reported as full text, published as abstract only, and unpublished data. We will exclude cross‐over trials, as they are not an appropriate design in this context. We will exclude quasi‐randomised trials and non‐randomised studies.

Types of participants

As an existing Cochrane Review has assessed the role of NPWT for open traumatic wounds (Iheozor‐Ejiofor 2018), we will not include trials involving participants with open abdomen caused by trauma. We will include trials involving adults managed in any care setting that used NPWT for the management of open abdomen caused by severe peritonitis after laparotomy. We will include people with open abdomen due to secondary ischaemic surgery, cancer surgery, and other procedures not for trauma. Trials involving both trauma and non‐trauma patients will be eligible only if the results for non‐trauma patients are presented separately and randomisation was stratified by trauma/non‐trauma, or if the majority of participants in the trial (75% or more) were non‐trauma patients. People who are undergoing abdominal wall correction months or years after initial management of the open abdomen will be excluded because in these cases the open abdomen is not treated during the first admission. Trials involving both first and subsequent admission patients will be eligible only if the results for first admission patients are presented separately and randomisation was stratified by first/subsequent treatments, or if the majority of participants in the trial (75% or more) were first admission patients.

Types of interventions

The primary intervention will be NPWT delivered by any mode. We will assess the following comparisons for people with an open abdomen not caused by trauma:

• NPWT (both commercial and non‐commercial products) versus an alternative method of temporary abdominal closure (e.g. Bogota bag, Wittmann patch, sterilised zipper, and synthetic mesh);

• one type of NPWT system versus a different type of NPWT system.

We will include RCTs in which the use of a specific NPWT intervention during the treatment period is the only systematic difference between treatment groups.

Types of outcome measures

We list primary and secondary outcomes below. If a study is otherwise eligible (i.e. correct study design, population, and intervention/comparator) but does not report a listed outcome, then we will contact the study authors where possible to establish whether an outcome of interest was measured but not reported. If the study authors reply and state that none of the outcomes were measured in their study, the study will be listed as an included study and the potential of selective outcome reporting will be discussed.

We will report outcome measures at the latest time point available (assumed to be length of follow‐up if not specified) and the time point specified in the study methods as being of primary interest (if this is different from the latest time point available). We will use the latest time point available for the primary analysis, and use the time point specified in the methods as being of primary interest as a sensitivity analysis. For all outcomes, we will class assessment of outcome measures from:

• less than one week to eight weeks as short term;

• greater than eight weeks to 26 weeks as medium term; and

• greater than 26 weeks as long term.

Primary outcomes

• Primary fascial closure of the abdomen.

• Adverse events.

Primary fascial closure

Primary fascial closure is defined as full fascia‐to‐fascia closure and complete wound closure after open abdominal treatment during index admission (hospital admission during which the open abdominal treatment was started). For this review, we will regard the following as providing the most relevant and rigorous measures of outcome:

• time to primary fascial closure of the abdomen. We will record whether or not censored data have been appropriately analysed, and list any adjustment factors;

• proportion of participants with wound with successful primary fascial closure of the abdomen (frequency of primary fascial closure) at a particular time point.

Where both of the outcomes above are reported, we will present all data in a summary outcome table for reference, but will focus on reporting time to primary fascial closure. We will accept authors' definitions of what constituted primary fascial closure. Time to primary fascial closure is our preferred measure; however, we do not expect it to be reported in many studies; if this is the case, we will extract and analyse time‐to‐event data but focus on the binary outcome in our conclusions.

Adverse events

Adverse events, including fistulae formation, hernia formation, intra‐abdominal abscess and failure to maintain negative pressure where a clear methodology for the collection of adverse event data was provided. We will report the number of participants in each group with an event.

Secondary outcomes

• All‐cause mortality.

• Participant health‐related quality of life/health status (measured using a standardised generic questionnaire such as EuroQol‐5D (EQ‐5D); 36‐item, 12‐item, or 6‐item Short Form (SF‐36, SF‐12, or SF‐6); or wound‐specific questionnaires such as the Cardiff Wound Impact Schedule). We will not include ad hoc measures of quality of life that are not likely to be validated and would not be common to multiple trials.

• Length of hospital stay.

• Reoperation rate.

• Wound infection: as defined by study authors (number of participants in each group with wound infection).

• Pain (measured using survey/questionnaire/data capture process or visual analogue scale).

Search methods for identification of studies

Electronic searches

We will search the following electronic databases to retrieve reports of relevant RCTs:

• the Cochrane Wounds Group Specialised Register;

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

• Ovid MEDLINE (from 1946 onwards);

• Ovid Embase (from 1974 onwards);

• EBSCO Cumulative Index to Nursing and Allied Health Literature (CINAHL Plus); from 1937 onwards.

We have devised a draft search strategy for CENTRAL which is displayed in Appendix 1. We will adapt this strategy to search the Cochrane Wounds Specialised Register, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL Plus. 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 2019). We will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2019). We will combine the CINAHL Plus search with the trial filter developed by Glanville 2019. There will be no restrictions of the searches by language, date of publication or study setting.

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

• WHO International Clinical Trials Registry Platform (www.who.int/trialsearch).

Searching other resources

We will search meeting abstracts via the Conference Proceedings Citation Index to explore further relevant clinical studies. We will contact corresponding authors and the manufacturers and distributors of NPWT systems. We will try to identify other potentially eligible trials or ancillary publications by searching the reference lists of retrieved included trials as well as relevant systematic reviews, meta‐analyses, and health technology assessment reports.

Data collection and analysis

Selection of studies

Two review authors (YC, JG) will independently assess the titles and abstracts of the citations retrieved by the searches for relevance. After this initial assessment, we will obtain full‐text copies of all studies considered to be potentially relevant. Two review authors (YC, JG) will independently check the full papers for eligibility; disagreements will be resolved by discussion and, where required, the input of a third review author. Where required and possible, we will contact study authors where the eligibility of a study is unclear. We will record all reasons for exclusion of studies for which we had obtained full copies in the 'Characteristics of excluded studies' table. We will complete a PRISMA flowchart to summarise this process (Liberati 2009).

Where studies have been reported in multiple publications/reports, we will obtain all publications. Where studies have multiple publications, we will collate the reports of the same study so that each study, rather than each report, is the unit of interest for the review, and such studies have a single identifier with multiple references. We will extract data from all reports to ensure maximal relevant data are obtained.

Data extraction and management

We will extract and summarise details of the eligible studies using a data extraction sheet. Two review authors (ZL, JG) will independently extract data and resolve disagreements by discussion, drawing on a third review author (ZZ) where required. Where data are missing from reports, we will attempt to contact the study authors to obtain this information. Where a study with more than two intervention arms is included, only data from intervention and control groups that meet the eligibility criteria will be extracted. Where a study with more than two eligible intervention arms is included, we will use either separate comparisons (with different forest plots) or will combine intervention groups where this is considered appropriate. This will avoid the double‐counting of participants.

We will extract the following data where possible by treatment group for the prespecified interventions and outcomes in this review and complete a 'Characteristics of included studies' table. Outcome data will be collected for relevant time points as described in Types of outcome measures:

• country of origin;

• type of surgery;

• trial design (e.g. parallel, cluster);

• care setting;

• number of participants randomised to each trial arm;

• eligibility criteria and key baseline participant data;

• details of treatment regimen received by each group;

• duration of treatment;

• details of any co interventions;

• primary and secondary outcome(s) (with definitions);

• outcome data for primary and secondary outcomes (by group);

• duration of follow‐up;

• number of withdrawals (by group);

• publication status of study; and

• source of funding for trial.

Assessment of risk of bias in included studies

Two review authors (YC, ZL) will independently assess included studies using the Cochrane 'Risk of bias' tool (Higgins 2017). This tool addresses six specific domains: sequence generation, allocation concealment, blinding, incomplete data, selective outcome reporting, and other issues. We will record issues with unit of analysis, for example where a cluster trial has been undertaken but analysed at the individual level in the study report (Appendix 1). We will assess blinding and completeness of outcome data for each of the review outcomes separately. We note that, since primary fascial closure is a subjective outcome, it can be at high risk of measurement bias when outcome assessment is not blinded. We will present our assessment of risk of bias using two 'Risk of bias' summary figures: a summary of bias for each item across all studies, and a summary of bias for each trial across all of the 'Risk of bias' items. If we judge a trial to be at low risk of bias in all domains, we will consider it to be at low risk of bias overall. We will consider trials to be at high risk of bias if they are judged to be at high risk of bias for one or more domains, or if the risk of selection bias or performance and detection bias is judged to be unclear.

For trials using cluster randomisation, we will also consider the risk of bias in terms of: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and comparability with individually randomised trials (Higgins 2019a) (Appendix 2).

Measures of treatment effect

For dichotomous outcomes, we will calculate the risk ratio (RR) with 95% confidence intervals (CI). For continuously distributed outcome data, we will use the mean difference (MD) with 95% CIs, if all trials use the same or similar assessment scale. If trials use different assessment scales, we will use the standardised mean difference (SMD) with 95% CIs. We will only consider mean or median time to primary fascial closure without survival analysis as a valid outcome if reports specify that all open abdomen wounds healed (i.e. if the trial authors regarded time to primary fascial closure as a continuous measure as there is no censoring). We will report time‐to‐event data (e.g. time‐to‐primary fascial closure) as hazard ratios (HR) and 95% CI where possible in accordance with the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2019). If studies reporting time‐to‐event data (e.g. time to primary fascial closure) do not report an HR, then, where feasible, we will estimate this using other reported outcomes, such as the numbers of events, through the application of available statistical methods (Parmar 1998).

Unit of analysis issues

We expect that the unit of analysis in most trials will be one participant with one abdominal wound subjected to one intervention. For such trials, we will treat the participant as the unit of analysis when the number of abdominal wound assessed appears equal to the number of participants (e.g. abdominal wound per participant). However, we anticipate the following two types of unit of analysis issues.

First, there may be trials where multiple abdominal wounds are associated with one or more participants. Here, the participant is randomised to an intervention (where all of their abdominal wounds receive this intervention), and instead of focusing on the individual, the analysis is conducted at the level of the abdominal wound. Such a trial would generate clustered data. However, many cluster‐randomised trials are incorrectly analysed as if randomisation was performed on individuals rather than clusters. We will record where a cluster‐RCT has been conducted but incorrectly analysed. This will be recorded as part of the 'Risk of bias' assessment. If possible, we will approximate the correct analyses based on guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019b), using information on:

• the number of clusters (or groups) randomised to each intervention group, or the mean size of each cluster;

• the outcome data ignoring the cluster design for the total number of participants (e.g. number or proportion of participants with events, or means and standard deviations); and

• an estimate of the intracluster (or intraclass) correlation coefficient (ICC).

If we cannot analyse the trial data correctly, we will extract and present outcome data but not analyse them further.

Second, there may be trials where individuals have multiple abdominal wounds and abdominal wounds are randomised to different interventions. When this is the case, we will note that randomisation has been undertaken at the abdominal wound level and will assess whether correct paired analysis was performed. If an incorrect analysis was performed, and if the required data can be accessed by contacting the study authors, we will try and approximate a correct analysis. If this is not possible, we will extract and present the relevant outcome data but not analyse or pool them further (Lesaffre 2009).

Dealing with missing data

It is common to have data missing from trial reports. Excluding participants post randomisation from the analysis, or ignoring those participants who are lost to follow‐up compromises the randomisation, and potentially introduces bias into the trial. Where there are missing data we consider should be included in the analyses, we will contact the study authors to request whether these data are available.

Where data remain missing for the 'proportion of participants with wound with successful primary fascial closure' outcome, for analysis we will assume that if randomised participants were not included in an analysis, their abdominal wound did not close (i.e. they would be considered in the denominator but not the numerator).

For continuous variables (e.g. length of hospital stay), and for all secondary outcomes, we will present available data from the study reports/study authors and do not plan to impute missing data. Where measures of variance are missing, we will calculate these wherever possible. If calculation is not possible, we will contact the study authors. Where these measures of variance are not available, we will exclude the study from any relevant meta‐analyses that are conducted.

Assessment of heterogeneity

Assessment of heterogeneity can be a complex, multi‐faceted process. First, we will consider clinical and methodological heterogeneity: that is, the degree to which the included studies vary in terms of participant, intervention, outcome, and characteristics such as length of follow‐up. This assessment of clinical and methodological heterogeneity will be supplemented by information regarding statistical heterogeneity – assessed using the Chi² test (a significance level of P < 0.10 will be considered to indicate statistically significant heterogeneity) in conjunction with the I² statistic (Higgins 2003). The I² statistic examines the percentage of total variation across RCTs that is due to heterogeneity rather than chance (Higgins 2003). In general, I² values of 25%, or less, may mean a low level of heterogeneity (Higgins 2003), and values of more than 75% indicate very high heterogeneity (Deeks 2019). Where there is evidence of high heterogeneity, we will attempt to explore this further: see Data synthesis.

Assessment of reporting biases

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. Publication bias is one of several possible causes of 'small‐study effects', that is, a tendency for estimates of the intervention effect to be more beneficial in smaller RCTs. Funnel plots allow a visual assessment of whether small‐study effects may be present in a meta‐analysis. A funnel plot is a simple scatter plot of the intervention effect estimates from individual RCTs against some measure of each trial's size or precision (Page 2019). We will present funnel plots for meta‐analyses comprising 10 RCTs or more using Review Manager 5 (Review Manager 2020).

Data synthesis

We will combine details of included studies in a narrative review according to type of comparator, possibly by aetiology of wound and then by outcomes by time period. We will consider clinical and methodological heterogeneity and undertake pooling when studies appear appropriately similar in terms of wound aetiology, intervention type, duration of follow‐up, and outcome type.

We are unable to pre specify the amount of clinical, methodological, and statistical heterogeneity in the included studies but it might be extensive. Thus, we anticipate using a random‐effects approach for meta‐analysis. Conducting meta‐analysis with a fixed‐effect model in the presence of even minor heterogeneity may provide overly narrow CIs. We will only use a fixed‐effect approach when clinical and methodological heterogeneity is assessed to be minimal, and the assumption that a single underlying treatment effect is being estimated holds. We will use Chi² and I² tests to quantify heterogeneity, but we will not use these to guide choice of model for meta‐analysis. We will exercise caution when meta‐analysed data are at risk of small‐study effects because a random‐effects model may be unsuitable. In this case, or where there are other reasons to question the selection of a fixed‐effect or random‐effects model, we will assess the impact of the approach using sensitivity analyses to compare results from alternate models. We will report any evidence that suggests that the use of a particular model might not be robust. We may meta‐analyse even when there is thought to be extensive heterogeneity. We will attempt to explore the causes behind this using meta‐regression, if possible (Thompson 1999).

We will present data using forest plots where possible. For dichotomous outcomes, we will present the summary estimate as an RR with 95% CI. Where continuous outcomes are measured in the same way across studies, we plan to present a pooled MD with 95% CI; we plan to pool SMD estimates where studies measure the same outcome using different methods. For time‐to‐event data, we plan to plot (and, if appropriate, pool) estimates of HRs and 95% CIs as presented in the study reports using the generic inverse variance method in Review Manager 5 (Review Manager 2020). Where time to primary fascial closure is analysed as a continuous measure but it is not clear if open abdomen healed, we will document use of the outcome in the study but we will not summarise data or use them in any meta‐analysis.

We will obtain pooled estimates of treatment effect using Review Manager 5 (Review Manager 2020).

'Summary of findings' tables

We will present the main results of the review in 'Summary of findings' tables. These tables present key information concerning the certainty of the evidence, the magnitude of the effects of the interventions examined, and the sum of the available data for the main outcomes (Schünemann 2019a). The 'Summary of findings' tables also include an overall grading of the evidence related to each of the main outcomes using the GRADE approach. The GRADE approach defines the certainty of a body of evidence as the extent to which one can be confident that an estimate of effect or association is close to the true quantity of specific interest. The certainty of a body of evidence involves consideration of within‐trial risk of bias (methodological quality), directness of evidence, heterogeneity, precision of effect estimates, and risk of publication bias (Schünemann 2019b). We plan to present the following outcomes in the 'Summary of findings' tables:

• time to primary fascial closure of the abdomen;

• proportion of participants with wound with successful primary fascial closure of the abdomen;

• adverse events;

• all‐cause mortality;

• participant health‐related quality of life.

We will consider the time‐points and method of outcome measurement specified in 'Types of outcome measures' in Summary of findings' tables. When evaluating the 'Risk of bias' domain, we will downgrade the GRADE assessment only when we classify a study as being at high risk of bias for one or more domains, or when the 'Risk of bias' assessment for selection bias (generation of the randomisation sequence domain and the allocation concealment domain) is unclear. We will downgrade the GRADE assessment when the 'Risk of bias' assessment for blinding is unclear (i.e. classified as unclear for the performance bias domain and the detection bias domain) as well as at high risk of bias. We will not downgrade for unclear 'Risk of bias' assessments in other domains.

We plan to select an informal optimal information size of 300 for binary outcomes, following the GRADE default value. We will also follow GRADE guidance and downgrade twice for imprecision when there are very few events and CIs around effects included both appreciable benefit and appreciable harm.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses if there are sufficient studies. We will not perform subgroup analysis when the number of studies included in the meta‐analysis is fewer than 10.

• different methods of temporary abdominal closure in the comparator group (e.g. Bogota bag, Wittmann patch, zipper);

• different aetiologies (e.g. severe peritonitis, severe acute pancreatitis).

The following outcomes will be used in subgroup analyses:

• primary fascial closure (time to primary fascial closure and proportion of participants with wound with successful primary fascial closure);

• adverse events.

We will explore differences between subgroups using random‐effects meta‐regression, if possible.

We will use the formal Chi² test for subgroup differences to test for subgroup interactions. We will compare subgroups using the analysis option of the 'Test for Subgroup Differences' in Review Manager 5.4 (Review Manager 2020).

Sensitivity analysis

We plan, where possible and appropriate to perform sensitivity analyses to explore the effects of the following criteria:

• changing between worst‐case scenario analysis and best‐case scenario analysis for missing data; or

• excluding studies in which either the mean or standard deviation, or both, were imputed

• using the time point specified in the methods as being of primary interest.

The following outcomes will be used in sensitivity analyses:

• primary fascial closure (time to primary fascial closure and proportion of participants with wound with successful primary fascial closure);

• adverse events.

The Methods section of this protocol is based on a standard template used by Cochrane Wounds.

History

Protocol first published: Issue 8, 2020

Appendices

Appendix 1. Risk of bias assessment (individually randomised controlled trials)

1. Was the allocation sequence randomly generated?

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.

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: sequence generated by odd or even date of birth; sequence generated by some rule based on date (or day) of admission; sequence generated by some rule based on hospital or clinic record number.

Unclear risk of bias

Insufficient information about the sequence generation process provided to permit a judgement of low or high risk of bias.

2. Was the treatment allocation adequately concealed?

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.

High risk of bias

Participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias, such as allocation based on: use of an open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards (e.g. envelopes were unsealed, non‐opaque, or not sequentially numbered); alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure.

Unclear risk of bias

Insufficient information provided to permit a judgement of low or high risk of bias. 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.

3. Blinding – was knowledge of the allocated interventions adequately prevented during the study?

Low risk of bias

Any one of the following.

• No blinding, but the review authors judge that the outcome and the outcome measurement are 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.

• Either participants or some key study personnel were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias.

High risk of bias

Any one of the following.

• No blinding or incomplete blinding, and the outcome or outcome measurement 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.

• Either participants or some key study personnel were not blinded, and the non‐blinding of others likely to introduce bias.

Unclear risk of bias

Either of the following.

• Insufficient information to permit judgement of low or high risk of bias.

• The study did not address this outcome.

4. Were incomplete outcome data adequately addressed?

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 unlikely to be introducing bias).

• Missing outcome data are 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, a plausible effect size (difference in means or standardised difference in means) among missing outcomes is not enough to have a clinically relevant impact on the observed effect size.

• Missing data have been imputed using appropriate methods.

High risk of bias

Any one of the following.

• Reason for missing outcome data are likely to be related to the true outcome, with either an 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, a plausible effect size (difference in means or standardised difference in means) among missing outcomes is enough to induce a clinically relevant bias in the observed effect size.

• 'As‐treated' analysis done with a substantial departure of the intervention received from that assigned at randomisation.

• Potentially inappropriate application of simple imputation.

Unclear risk of bias

Either of the following.

• Insufficient reporting of attrition/exclusions to permit a judgement of low or high risk of bias (e.g. number randomised not stated, no reasons for missing data provided).

• The study did not address this outcome.

5. Are reports of the study free of suggestion of selective outcome reporting?

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).

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/are reported using measurements, analysis methods, or subsets of the data (e.g. subscales) that were not prespecified.

• One or more reported primary outcomes was/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 is/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.

Unclear risk of bias

Insufficient information provided to permit a judgement of low or high risk of bias. It is likely that the majority of studies will fall into this category.

6. Other sources of potential bias

Low risk of bias

The study appears free of other sources of bias.

High risk of bias

There is at least one important risk of bias. For example, the study:

• had a potential source of bias related to the specific study design used; or

• has been claimed to have been fraudulent; or

• had some other problem.

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.

Appendix 2. Risk of bias assessment (cluster randomised controlled trials)

In cluster randomised trials, particular biases to consider include: recruitment bias; baseline imbalance; loss of clusters; incorrect analysis; and comparability with individually randomised trials.

• Recruitment bias: can occur when individuals are recruited to the trial after the clusters have been randomised, as the knowledge of whether each cluster is an 'intervention' or 'control' cluster could affect the types of participants recruited.

• Baseline imbalance: cluster randomised trials often randomise all clusters at once, so lack of concealment of an allocation sequence should not usually be an issue. However, because small numbers of clusters are randomised, there is a possibility of chance baseline imbalance between the randomised groups, in terms of either the clusters or the individuals. Although not a form of bias as such, the risk of baseline differences can be reduced by using stratified or pair‐matched randomisation of clusters. Reporting of the baseline comparability of clusters, or statistical adjustment for baseline characteristics, can help reduce concern about the effects of baseline imbalance.

• Loss of clusters: occasionally complete clusters are lost from a trial, and have to be omitted from the analysis. Just as for missing outcome data in individually randomised trials, this may lead to bias. In addition, missing outcomes for individuals within clusters may also lead to a risk of bias in cluster randomised trials.

• Incorrect analysis: many cluster randomised trials are analysed by incorrect statistical methods, not taking the clustering into account. Such analyses create a 'unit of analysis error' and produce over‐precise results (the standard error of the estimated intervention effect is too small) and P values that are too small. They do not lead to biased estimates of effect. However, if they remain uncorrected, they will receive too much weight in a meta‐analysis.

• Comparability with individually randomised trials: in a meta‐analysis including both cluster and individually randomised trials, or including cluster randomised trials with different types of clusters, possible differences between the intervention effects being estimated need to be considered. For example, in a vaccine trial of infectious diseases, a vaccine applied to all individuals in a community would be expected to be more effective than if the vaccine was applied to only half of the people. Another example is provided by a Cochrane Review of hip protectors (Hahn 2005). The cluster trials showed large positive effects whereas individually randomised trials did not show any clear benefit. One possibility is that there was a 'herd effect' in the cluster randomised trials (which were often performed in nursing homes, where compliance with using the protectors may have been enhanced). In general, such 'contamination' would lead to underestimates of effect. Thus, if an intervention effect is still demonstrated despite contamination in those trials that were not cluster randomised, a confident conclusion about the presence of an effect can be drawn. However, the size of the effect is likely to be underestimated. Contamination and 'herd effects' may be different for different types of cluster.

Appendix 3. The Cochrane Central Register of Controlled Trials (CENTRAL) draft search strategy

#1 MeSH descriptor Negative‐Pressure Wound Therapy explode all trees

#2 MeSH descriptor Suction explode all trees

#3 MeSH descriptor Vacuum explode all trees

#4 ("negative pressure" or negative‐pressure or TNP):ti,ab,kw

#5 (sub‐atmospheric or subatmospheric):ti,ab,kw

#6 ((seal* NEXT surface*) or (seal* NEXT aspirat*)):ti,ab,kw

#7 (wound NEAR/3 suction*):ti,ab,kw

#8 (wound NEAR/3 drainage):ti,ab,kw

#9 ((foam NEXT suction) or (suction NEXT dressing*)):ti,ab,kw

#10 ((vacuum NEXT therapy) or (vacuum NEXT dressing*) or (vacuum NEXT seal*) or (vacuum NEXT assist*) or (vacuum NEAR closure) or (vacuum NEXT compression) or (vacuum NEXT pack*) or (vacuum NEXT drainage) or VAC):ti,ab,kw

#11 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8 OR #9 OR #10)

#12 MeSH descriptor Abdomen explode all trees with qualifier: SU

#13 MeSH descriptor Laparotomy explode all trees

#14 MeSH descriptor Abdominal Injuries explode all trees

#15 MeSH descriptor Abdominal Cavity explode all trees

#16 MeSH descriptor Abdominal Wall explode all trees

#17 ("open abdomen" or "open abdominal or "abdominal closure"):ti,ab,kw

#18 (#12 OR #13 OR #14 OR #15 OR #16 OR #17)

#19 (#11 AND #18)

Contributions of authors

Yao Cheng: developed the protocol; produced the first draft of the protocol; approved the final version of the protocol prior to publication; is guarantor of the protocol.

Junhua Gong: developed the protocol; approved the final version of the protocol prior to publication.

Zuojin Liu: conceived the review question; advised on the protocol; approved the final version of the protocol prior to publication.

Jianping Gong: contributed to writing and editing the protocol; approved the final version of the protocol prior to publication.

Zhong Zeng: secured funding; approved the final version of the protocol prior to publication.

Contributions of editorial base

Gill Norman (Editor): edited the protocol; advised on methodology, interpretation, and protocol content; approved the final protocol prior to publication.

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

Sophie Bishop (Information Specialist): designed the search strategy and edited the search methods section.

Tom Patterson (Editorial Assistant): checked the reference sections.

Sources of support

Internal sources

• No sources of support supplied

External sources

• The National Institute for Health Research (NIHR), UK

  This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to Cochrane Wounds. The views expressed are those of the authors and not necessarily those of the NIHR or the Department of Health and Social Care.

Declarations of interest

Yao Cheng: none known.

Junhua Gong: none known.

Zuojin Liu: none known.

Jianping Gong: none known.

Zhong Zeng: none known.

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