Drainage versus no drainage for lower limb arterial surgery

  • Protocol
  • Intervention



This is the protocol for a review and there is no abstract. The objectives are as follows:

To determine whether routine placement of drains can result in fewer complications following lower limb arterial surgery compared with non-placement of drains.


Surgical drains are frequently used in a wide range of surgical procedures, including lower limb arterial vascular surgery, despite a lack of firm evidence that they are beneficial (Barie 2002; Grobmyer 2002). Lower limb arterial surgery may be carried out electively, or as an emergency, to restore blood supply to the leg. The blood supply to the leg may be restricted due to partial blockages caused by the presence of an embolus (a substance formed from either a blood clot, air, fat or tumour tissue that is carried by the bloodstream) or a thrombus (blood clot attached to the wall of the artery), or by a condition known as atherosclerosis. In atherosclerosis an abnormal mass of fat, fibrous tissue and inflammatory cells (atheroma) within the artery combines with narrowing and hardening of the vessels (arteriosclerosis) to restrict blood flow. Blood flow blockages due to emboli or thrombi tend to be sudden in onset, whereas those blockages caused by atherosclerosis tend to occur gradually.

Surgical procedures to restore blood supply to the leg involve removing or bypassing the blockage. A thrombus or embolus can be removed by a thrombectomy or embolectomy procedure. If the blockage is caused by the slow build up of atheroma to a critical level, an endarterectomy may be performed. This is an operation in which a short deposit of atheroma is removed, thus improving blood flow. If removing the blockage is not a suitable option, the blockage may be bypassed using a graft. Grafts can be made of synthetic material or can be autologous (i.e. a portion of the patient's own vein). In some cases peripheral angioplasty - a technique in which narrowed or obstructed arteries are widened mechanically - is used in conjunction with surgical treatment. In this procedure, a collapsed balloon, known as a balloon catheter, is passed with X-ray guidance into the artery along a guide wire to the site of the obstruction. The balloon is inflated to open up the blood vessel for improved flow, then the balloon is deflated and withdrawn (Grace 1996)

Description of the condition

Peripheral arterial occlusive disease (PAOD), also known as peripheral vascular disease (PVD), refers to narrowing or blockage of the blood vessels bringing blood from the heart to distant parts of the body. PVD can occur in any blood vessel, but it most commonly affects the lower limbs. It is usually caused by atherosclerosis, although rare causes also exist. These rare causes include blockages caused by recurrent small emboli or arteritis (inflammation of the artery). People with PVD present with signs and symptoms that vary according to the severity of the arterial blockage and the subsequent reduction in arterial blood supply (ischaemia). Symptoms range from none, to intermittent claudication (leg pain when walking that is relieved by rest), to pain at rest, ulceration or gangrene (tissue death). Data from the National Health and Nutrition Examination Survey in the USA, report the prevalence of PVD in the general population as being 12% to 14%, with prevalence increasing to 20% in those over 75 years of age. Amongst those affected, 70% to 80% are asymptomatic, and only a minority require revascularisation (a procedure to restore blood supply) (Ostchega 2007; Selvin 2007; Shammas 2007). The incidence of symptomatic PVD increases with age, from about 0.3% per year for men aged 40 to 55 years, to about 1% per year for men aged over 75 years (Shammas 2007).

Lower limb arterial surgery is performed to restore blood flow to legs that are affected by acute or chronic ischaemia when non-operative treatment has not been successful (Grace 1996). These procedures are often complicated by groin haematomas (localised collection of blood outside blood vessels, within the tissue), lymphoceles (a collection of lymphatic fluid that can result from damage to lymph vessels during surgery), or seromas (a pocket of clear serous fluid that develops after surgery) (Youssef 2005; Karthikesalingam 2008).These complications can lead to infection, with resulting failure of vein grafts, and therefore should be avoided if possible (Youssef 2005; Karthikesalingam 2008).

Description of the intervention

Drains serve to remove blood, lymph, serum and other fluids that can accumulate in the wound bed after an operation. If allowed to collect, these fluids can form haematomas, seromas and lymphoceles that can put pressure on the surgical site and adjacent organs, vessels, and nerves. This increased pressure can cause additional pain, and reduce the delivery of blood to the micro vessels (reduced perfusion), which impairs healing. Accumulated fluid can also increase the risk of infection. The practice of placing drains routinely to safeguard against complications in surgical wound management following lower limb arterial surgery remains widespread (Grobmyer 2002). Some units employ a selective policy of using drains if there have been concerns over haemostasis (stopping bleeding) intra-operatively, while others use drains routinely (Karthikesalingam 2008). Drains can rely on pressure and gravity to help drainage (passive drainage), or can be helped by a suction mechanism (active drainage). Fluids can be removed from a wound using either open or closed systems. An open drain depends on gravity to remove fluid from a wound site into a wound dressing placed over the end of the drain; examples include corrugated, Penrose and Yeates drains. A closed drainage system consists of a tube left in the wound that drains fluids from the body into a closed container. Closed drains may be assisted by suction or a vacuum, as in the Redon or Jackson-Pratt drains. The type of drain upon which a surgeon decides depends upon the location of the operative site and the amount of drainage expected. In certain procedures the use of drains has been shown to be of no benefit, and it has been suggested they may cause harm to the patient (for instance providing a portal for invasion by bacterial pathogens) (Barie 2002). Open drains are associated with an increased risk of infection, as, not only do they provide a portal for infection, but they also provide the potential for drained fluid to come into contact with, and so contaminate, the incision site. They should be avoided, particularly if a prosthesis is present (Smith 1985). Debate regarding the use of drains following lower limb arterial surgery is on-going; this review aims to clarify the benefits and harms of this intervention to this patient group.

How the intervention might work

The potential benefits of drainage are many, and include prevention of fluid collections, reduction of infections and earlier identification of bleeding (Youssef 2005). Conversely, drains may cause infection due to delayed wound closure, and may prolong hospital stay (Karthikesalingam 2008).

Why it is important to do this review

The benefits of routine drainage have not materialised to the degree that one might expect, with numerous studies from a wide range of specialties suggesting that routine drainage is not advantageous (Karliczek 2006; Gurusamy 2007a; Gurusamy 2007b; Gurusamy 2007c; Hellums 2007; Parker 2007; Samraj 2007; Clifton 2008; Charoenkwan 2010; Diener 2011; Wang 2011; Zhang 2011; Gurusamy 2012). It is unclear whether routine placement of surgical drains is of benefit in lower limb arterial surgery. Currently, there are no formal guidelines for usage of drains following arterial surgery. A systematic review on this topic was published in 2008 (Karthikesalingam 2008) and concluded there was no clear evidence that closed-suction drainage reduced complications following lower limb revascularisation. The review included data from only four small trials which, combined with an absence of information on data extraction and validity assessment, limits the reliability of the findings. This review aims to provide a definitive appraisal of the evidence on drainage in lower limb arterial surgery. We aim to provide vascular surgeons with robust data, from a thorough evaluation of the literature, upon which to base their drain-usage policy. In addition it is hoped this review will provide policy makers with the evidence to support, or limit, this practice.


To determine whether routine placement of drains can result in fewer complications following lower limb arterial surgery compared with non-placement of drains.


Criteria for considering studies for this review

Types of studies

We will consider randomised controlled trials (RCTs) that evaluate the use of any type of drain in lower limb arterial surgery. Cross-over trials will not be appropriate due to the short-term nature of the condition under investigation, and are unlikely to be encountered; they will not be included. Quasi-randomised controlled trials will also be excluded. If cluster trials are encountered, the data will be included in the meta-analysis, and a sensitivity analysis will be undertaken to evaluate the effect of the cluster trial(s) on the final results. A study follow-up period of one year or less will be applied for the purpose of the review to allow for the reporting of longer-term outcomes such as wound infection.

Types of participants

We will consider trials that recruited people undergoing elective or emergency lower limb arterial surgery (bypass with synthetic or autologous graft; endarterectomy with or without angioplasty; embolectomy; thrombectomy).

Types of interventions

This review will compare the placement of any surgical drain following lower limb arterial surgery with routine closure with no surgical drain. Trials comparing different types of drains (e.g. closed versus open drains; suction versus non-suction drains) will be included as separate subgroups within the review. There will be no restriction regarding the location of wounds.

Types of outcome measures

Primary outcomes
  • Incidence of any surgical site infection (superficial and / or deep); incidence of all types of surgical site infection (if type not specified). Surgical site infection: as defined by the Centers for Disease prevention and Control (CDC)(Mangram 1999), is an infection that occurs within 30 days after surgery in the part of the body where the surgery took place. Surgical site infections can be superficial, involving the skin only, or they can be deep, involving tissues under the skin, organs, or implanted material (Mangram 1999).

Secondary outcomes
  • Incidence of wound dehiscence: defined as rupture of the wound suture line after surgery.

  • Incidence of fluid collections: defined as a collection of either serous or lymphatic fluid within the tissue (seroma and lymphocoele respectively).

  • Incidence of haematoma formation: defined as a localised collection of blood outside the blood vessels, within the tissue.

  • Incidence of graft occlusion: defined as a blockage of the bypass graft that limits blood flow.

  • Incidence of reoperation for wound or graft-related complications.

  • Length of hospital stay.

  • Change in health-related quality of life between pre-operative baseline and within 30 days post-operatively. Data generated using validated generic instruments (e.g. EQ-5D, SF-36, SF-12 or SF-6D) or validated wound-specific instruments will be used.

  • Mortality (all cause).

The definition of each outcome will be extracted from each study included in this review and this information will be recorded and reported.

Summary of findings

A summary of findings table will present key information relating to the quality of evidence, the size of the effects of the interventions examined and the sum of the available data for the main outcomes (Schünemann 2011a). The summary of findings tables will also grade the evidence related to each of the main outcomes using the GRADE assessment (Grading of Recommendations Assessment, Development and Evaluation) approach (Schünemann 2011b). The GRADE approach defines the strength 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. Quality 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 2011b). We plan to present the following outcomes in the ’Summary of findings’ tables:

  • Wound infection.

  • Wound dehiscence

  • Reoperation for wound or graft-related complications.

  • Changes in health-related quality of life.

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 Group Specialised Register;
• The Cochrane Central Register of Controlled Trials (CENTRAL) (latest issue);
• Ovid MEDLINE (1946 to present);
• Ovid EMBASE (1974 to present);
• EBSCO CINAHL (1982 to present)

We will use the following search strategy in the Cochrane Central Register of Controlled Trials (CENTRAL):

#1 MeSH descriptor: [Vascular Surgical Procedures] explode all trees
#2 MeSH descriptor: [Lower Extremity] explode all trees
#3 #1 and #2
#4 MeSH descriptor: [Leg] explode all trees
#5 #1 and #4
#6 MeSH descriptor: [Groin] explode all trees
#7 (lower limb* near/5 (arterial surgery or artery surgery or revasculari?ation)):ti,ab,kw
#8 (lower extremit* near/5 (arterial surgery or artery surgery or revasculari?ation)):ti,ab,kw
#9 (leg* near/5 arterial surgery):ti,ab,kw
#10 MeSH descriptor: [Femoral Artery] explode all trees
#11 femoral arter* surgery:ti,ab,kw
#12 (endarterectomy near/5 (leg* or lower extremit*)):ti,ab,kw
#13 (thrombectomy or embolectomy or peripheral arterial bypass):ti,ab,kw
#14 {or #3, #5-#13}
#15 MeSH descriptor: [Drainage] explode all trees
#16 MeSH descriptor: [Suction] explode all trees
#17 drain*:ti,ab,kw
#18 {or #15-#17}
#19 #14 and #18

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 searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2013). We will not restrict studies with respect to language or date of publication or study setting.

We will also search the following online clinical trial registries;

  • The US National Institutes of Health registry (www.clinicaltrials.gov)

  • The EU Clinical Trials Register (www.clinicaltrialsregister.eu)

  • Current Controlled Trials Register (www.controlled-trials.com)

  • The World Health Organization International Trial Registry Platform (www.who.int/ictrp/en/)

  • The International Standard Randomised Controlled Trial Number (ISRCTN) register (www.controlled-trials.com/isrctn/)

Searching other resources

We will attempt to contact trialists to obtain unpublished data and information as required. We will also search the reference lists of other systematic reviews and the reference lists of included trial reports.

Data collection and analysis

Selection of studies

Independently, two review authors will assess the titles and abstracts of papers retrieved by the searches and review their relevance. After this initial assessment, we will obtain full texts of those trials thought to be potentially relevant. Independently, two review authors will then check the full papers for eligibility, with disagreements resolved by discussion and, where required, referral to the third review author. We will record all reasons for exclusion.

Data extraction and management

Details of eligible studies will be extracted and summarised using a data extraction table. Two review authors (DH and MCM) will independently extract and summarise details of the eligible trials and enter the details into a review-specific spreadsheet template, after which both data extractions will be compared for agreement. We will resolve any disagreements by discussion. If data are missing from reports we will attempt to contact the trial authors to obtain the missing information. We will include trials published as duplicate reports (parallel publications) once, using all associated trial reports to extract the maximum amount of trial information, but ensuring that the trial data are not duplicated in the review. We will extract the following information in addition to the specific outcomes already listed.

  • Trial authors.

  • Year of publication.

  • Country in which trial was undertaken.

  • Setting of care.

  • Participant characteristics (selection criteria and baseline characteristics).

  • Trial design (e.g. pragmatic RCT, cluster RCT).

  • Overall sample size and methods used to estimate statistical power.

  • Unit of investigation.

  • Number of participants allocated per group.

  • Intervention regimens and comparators (characteristics of drains used, duration of drainage, co-interventions such as antibiotics).

  • Outcomes (assessment methods and data per group).

  • Withdrawal (numbers per group and reasons).

  • Risk of bias criteria

Assessment of risk of bias in included studies

Independently, two review authors will apply the Cochrane Collaboration’s tool for assessing risk of bias to each included study (Higgins 2011a). This tool addresses six specific domains: sequence generation; allocation concealment; blinding; incomplete outcome data; selective outcome reporting; and other issues. The criteria used to define level of bias as high risk, low risk or unclear risk of bias are detailed in Appendix 1. Different issues arise when considering bias in any cluster-randomised trials which are encountered (Higgins 2011b). The evaluation of bias in cluster-randomised trials is detailed in Appendix 2.

Studies which are judged to be at low risk of bias overall will be those which have low risk of bias for all three key domains of random sequence generation, allocation concealment and reporting of follow-up. Similarly a study will have to have all three key domains rated as low risk individually to be rated as low risk of bias overall.

We will present our assessment of risk of bias findings using a ’Risk of bias’ summary figure, which presents all of the judgements in a cross-tabulation of trials. This display of internal validity indicates the weight the reader may give the results of each trial.

Measures of treatment effect

For dichotomous variables, we will calculate risk ratios (RR) with 95% confidence intervals (CI). For continuous variables, we will calculate the mean difference (MD) with 95% CIs.

Unit of analysis issues

Lower limb revascularisation procedures often result in multiple wounds. Thus, some trials may use the number of wounds as the trial denominator, rather than the number of participants randomised into the group concerned. For the purposes of meta-analysis, a participant who develops any number of wound complications will be considered to have had one outcome. The number of participants randomised will be used as the group denominator, rather than the number of wounds in the group . For example, if a trial reports that three participants with nine wounds between them in a group of 20 randomised participants each develops complications in two of their wounds (six wound complications in total), then, for meta-analysis, the number of patients with a wound complication (three) will be used as the numerator while the total number of patients randomised in the group (20) will be used as the denominator. This will prevent unit of analysis errors in the meta-analysis. A comparison between the events reported in each trial and those calculated for the meta-analysis will be included in the discussion. The comparison will explore whether the original trials appropriately accounted for multiple events in individual patients (which are non-independent) and whether this influenced the original trial results. A further issue may arise if only the number of wounds randomised is available, with no data regarding the number of participants in each arm. This raises the possibility that individual patients may have some wounds with drains and some without. Outcomes from each wound in a given patient would not be independent, despite their allocation to separate arms of the trial. Therefore, trials in which only the number of wounds randomised is available will be excluded from the main analysis. If this situation arises, a sensitivity analysis will be undertaken in which the excluded trials are added to the main analysis to determine if these trials have any influence on the treatment effect estimate.

Dealing with missing data

Primary trial authors will be contacted to obtain any missing data. Where missing data remain unavailable we will present and analyse information as available from the trial report (i.e. complete case data).

Assessment of heterogeneity

We will consider clinical and statistical heterogeneity. Statistical pooling will only be considered for groups of RCTs with similar participant, intervention and outcome characteristics. As clinical heterogeneity is typical of surgical trial populations, particularly in terms of the number of different surgeons and the varying severity of disease, we will take this into account when considering if it is appropriate to combine trials. We will initially investigate statistical heterogeneity between comparable trials (where trials appear similar in terms of number of participants, intervention type and outcome type) by visual inspection of the forest plot. The Chi2 test (P value < 0.1) will be used to test for the presence of statistically significant statistical heterogeneity between effect sizes of included studies. The degree of inconsistency between trials will be estimated using the I2 statistic. A value of I2 greater than 50% will be considered to represent substantial heterogeneity (Deeks 2011) and we will explore heterogeneity and possible reasons.

Assessment of reporting biases

A funnel plot will be constructed to estimate publication bias. Funnel plots will only be constructed if there are at least ten studies to be included in a meta-analysis.

Data synthesis

We will present a narrative overview of all included RCTs, with results grouped according to the type of drain used (open or closed) and the comparator characteristics. Data will be entered into Revman (version 5.2) and analysis undertaken in accordance with published guidelines (Deeks 2011). An overall comparison of any drain versus no drain will be undertaken as the main analysis; comparisons between different types of drains will be conducted as secondary analyses. Results will be presented with 95% confidence intervals (CI). Estimates for dichotomous outcomes (e.g. wound infection - yes or no) will be reported as a pooled risk ratio (RR) (Deeks 2011). Continuous data (e.g. length of hospital stay) will be presented as a pooled mean difference (MD). The standardised mean difference (SMD) will be considered for pooling continuous data when RCTs use a variety of instruments to assess a common underlying concept (e.g. change in health-related quality of life). In the absence of clinical and statistical heterogeneity a fixed effects model will be applied to pool data where pooling is appropriate (i.e. I2 equal to, or less than 50%). In the presence of statistically significant statistical heterogeneity (as demonstrated by the Chi-squared test p<0.10) a random effects model will be applied for meta-analysis. Where synthesis is inappropriate (i.e. I2 greater than 50%) we will refrain from pooling. The results of each model will be presented in a forest plot and an overall summary results table. We will not combine data across outcomes.

Subgroup analysis and investigation of heterogeneity

If possible, we will undertake a subgroup analysis to evaluate the effect of revision surgery (surgery requiring re-opening of a healed wound) on the harms or benefits of drains.

Sensitivity analysis

Treatment effects may differ between cluster-randomised and individual-randomised trials. In some instances, large positive or negative treatment effects in cluster-randomised trials may outweigh the results of individual-randomised trials. To account for this, if we encounter cluster trials, we will perform a sensitivity analysis to evaluate their impact on the pooled treatment effect estimates. We will conduct a further sensitivity analysis to include those studies that adhere to the strict CDC definition of wound infection within 30 days of surgery (Mangram 1999). We will undertake a third sensitivity analysis to evaluate the influence of the risk of bias on effect sizes; we will assess the influence of removing of studies classed at high and unclear risk of bias from meta-analyses. We will only include studies that are assessed as having a low risk of bias in all key domains, namely adequate generation of the randomisation sequence, adequate allocation concealment and blinding of outcome assessor, for the estimates of treatment effect. Clarification of the definitions in these contexts is provided in Appendix 1.


We are very grateful to the following peer referees who provided valuable feedback on the draft protocol: Sonya Osborne, Ruth Foxlee, Anne-Marie Bagnall, Evangelos Kontopantelis, Karen Woo and Ann Lyddiattl. We should like to express appreciation for all the support we have received from the staff of the Cochrane Wounds Group - in particular to Ruth Foxlee for advising on the search strategy and to Sally Bell-Syer for her helpful advice and assistance in preparing the draft protocol.


Appendix 1. Risk of bias’ criteria

’Risk of bias’ criteria

1.Was 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 to permit a judgement of low or high risk of bias to be made.

2. Was 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: 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 non-opaque or not sequentially-numbered); alternation or rotation; date of birth; case record number; or any other explicitly unconcealed procedure.
Unclear risk of bias: insufficient information to permit a judgement of low or high risk of bias to be made. This is usually the case if the method of concealment is not described, or not described in sufficient detail to allow a definite judgement to be made, for example if the use of assignment envelopes is described, but it remains unclear whether envelopes were sequentially-numbered, opaque and sealed.

3. Blinding of participants and personnel - was knowledge of allocated interventions adequately prevented during the study period?

Low risk of bias: no blinding, but the review authors judge that the outcome and the outcome measurement are not likely to be influenced by lack of blinding or blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken.
High risk of bias: no blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding, or 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.
Unclear risk of bias: insufficient information to permit a judgement of low risk or high risk to be made, or the study did not address this outcome.

4. Blinding of outcome assessment - was knowledge of allocated interventions adequately prevented during the study period?

Low risk of bias: no blinding of outcome assessment, but the review authors judge that the outcome measurement is not likely to be influenced by lack of blinding or blinding of outcome assessment ensured, and unlikely that the blinding could have been broken.
High risk of bias: no blinding of outcome assessment, and the outcome measurement is likely to be influenced by lack of blinding or 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.
Unclear risk of bias: insufficient information to permit a judgement of low risk or high risk to be made, or the study did not address this outcome.

5. Were incomplete outcome data adequately addressed?

Low risk of bias: no missing outcome data, or reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias), or missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; or (for dichotomous (categorical) outcome data), the proportion of missing outcomes compared with observed event risk was not enough to have a clinically relevant impact on the intervention effect estimate; or (for continuous outcome data), plausible effect size (difference in means or standardised difference in means) among missing outcomes was not enough to have a clinically relevant impact on observed effect size; or missing data have been imputed using appropriate methods
High risk of bias: any one of the following; not all of the study’s pre-specified primary outcomes have been reported; one or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not pre-specified; one or more reported primary outcomes were not pre-specified (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.
Unclear risk of bias: insufficient information to permit a judgement of low or high risk of bias to be made. It is likely that the majority of studies will fall into this category.

6. Other

People undergoing revision arterial surgery may be at higher risk of wound complications. Trials that excluded people undergoing revision surgery or that included them but used stratified randomisation to distribute them across the trial groups will be classed as being at low risk of bias. Trials in which the inclusion or exclusion of revision patients is unclear, or not stated, will be classed as being at unclear risk of bias. Trials that included revision patients, but did not stratify or provide a subgroup analysis for the revision surgery group, will be classified as being at high risk of bias.

Appendix 2. Risk of bias criteria for cluster-randomised trials

1. Is there evidence of possible recruitment bias?

Recruitment bias may occur in cluster-randomised trials when participants are recruited after randomisation of the cluster. Given the nature of the intervention (drain placement following arterial surgery), it is highly likely that participants will be recruited following cluster randomisation in any cluster-randomised trials that are encountered. The possibility of differential recruitment will be considered for each trial by examining the baseline characteristics of participants recruited in each cluster to ascertain whether there were imbalances in major risk factors for wound complications e.g. obesity, diabetes, revision surgery. Trials in which the intervention (drain) clusters contain a disproportionate number of low-risk patients or in which control (no drain) clusters contain a disproportionate number of high-risk participants will be considered 'high-risk' for recruitment bias.

2. Is there evidence of baseline imbalance?

Cluster trials will be examined to determine if there were baseline differences between clusters. Trials in which the baseline characteristics of the clusters were not reported or which did not undertake statistical adjustment for baseline imbalances will be considered 'high-risk' for baseline imbalance.

3. Were clusters lost?

Loss of an entire cluster or loss of follow-up of individuals within a cluster introduces a risk of bias into the trial results.

4. Incorrect analysis.

Cluster-randomised trials will be examined to determine if appropriate statistical analysis (correcting for the effect of clustering) was undertaken. Trials which have not corrected for clustering will yield over-precise effect size estimates, which could bias meta-analysis.

5. Comparabilty with individually randomised trials

The results from any cluster trials will be compared to the results of individually randomised trials to determine whether there are any differences in the treatment effects being estimated. Any reasons for such differences will be explored.

Contributions of authors

Stewart Walsh: conceived the review question, co-ordinated the development, performed part of the writing or editing, made an intellectual contribution to, advised on, acted as guarantor for and approved final version of the protocol prior to submission.
Donagh Healy: developed, completed the first draft of, and made an intellectual contribution to the protocol.
Mary Clarke-Moloney: developed, edited, made an intellectual contribution to, and approved final version of the protocol prior to submission.

Contributions of editorial base:

Susan O'Meara, Editor: edited the protocol; advised on methodology, interpretation and protocol content. Approved the final protocol prior to submission.
Sally Bell-Syer: coordinated the editorial process. Advised on methodology, interpretation and content. Edited the protocol.
Ruth Foxlee: designed the search strategy and edited the search methods section.

Declarations of interest

Stewart Walsh: none known
Donagh Healy: none known
Mary Clarke-Moloney: none known

Sources of support

Internal sources

  • No sources of support supplied

External sources

  • The National Institute for Health Research (NIHR) is the sole funder of the Cochrane Wounds Review Group, UK.