Use of plastic adhesive drapes during surgery for preventing surgical site infection (2024)

PMCID: PMC6575154

Joan Webster, Email: moc.dnopgib@3491nagiw, Email: moc.dnopgib@3491nagiw.

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This article is an update of "Use of plastic adhesive drapes during surgery for preventing surgical site infection." onpageCD006353.

Background

Surgical site infection has been estimated to occur in about 15% of clean surgery and 30% of contaminated surgery cases. Using plastic adhesive drapes to protect the wound from organisms that may be present on the surrounding skin during surgery is one strategy used to prevent surgical site infection. Results from non‐randomised studies have produced conflicting results about the efficacy of this approach. A systematic review was required to guide clinical practice.

Objectives

To assess the effect of adhesive drapes used during surgery on surgical site infection, cost, mortality and morbidity.

Search methods

For this fourth update we searched the Cochrane Wounds Group Specialised Register (searched 4th March 2015); the Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library 2015, Issue 2); Ovid MEDLINE (2012 to 3rd March 2015); Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations, 2012 to 3rd March 2015); Ovid EMBASE (2012 to 3rd March 2015); and EBSCO CINAHL (2012 to 4th March 2015).

Selection criteria

Randomised controlled trials comparing any plastic adhesive drape with no plastic adhesive drape, used alone or in combination with woven (material) drapes or disposable (paper) drapes, in patients undergoing any type of surgery. Ring drapes were excluded.

Data collection and analysis

Two review authors independently selected and assessed studies for trial quality and both independently extracted data. We contacted study authors for additional information.

Main results

We identified no new studies for this fourth update. The review includes five studies involving 3082 participants comparing plastic adhesive drapes with no drapes and two studies involving 1113 participants comparing iodine‐impregnated adhesive drapes with no drapes. A significantly higher proportion of patients in the adhesive drape group developed a surgical site infection when compared with no drapes (risk ratio (RR) 1.23, 95% confidence interval (CI) 1.02 to 1.48, P = 0.03). Iodine‐impregnated adhesive drapes had no effect on the surgical site infection rate (RR 1.03, 95% CI 0.06 to 1.66, P = 0.89). Length of hospital stay was similar in the adhesive drape and non‐adhesive drape groups.

Authors' conclusions

There was no evidence from the seven trials that plastic adhesive drapes reduce surgical site infection rates, and some evidence that they increase infection rates. Further trials may be justified, using blinded outcome assessment to examine the effect of adhesive drapes on surgical site infection, based on different wound classifications.

Types of studies

We included randomised controlled trials (RCTs) that evaluated the effectiveness of adhesive drapes (used alone or in combination with other drapes), in preventing SSI.

Types of participants

We considered for inclusion, trials recruiting people of any age or gender, undergoing any type of inpatient or outpatient surgery.

Types of interventions

The primary intervention was adhesive drapes (polyethylene, polyurethane or polyvinyl), through which an incision is made. Adhesive drapes may have been used alone or in combination with other drapes: woven (material) drapes or disposable (paper) drapes and with any antiseptic skin preparation. The comparison intervention was no adhesive drapes; other drapes such as woven (material) drapes or disposable (paper) drapes may have been used. We excluded trials evaluating plastic 'ring drapes' or 'V' drapes as the incision is not made through the drape.

Comparisons included:

• adhesive drapes (without added antimicrobial properties) compared with no adhesive drapes; and

• adhesive drapes (with added antimicrobial properties) compared with no adhesive drapes.

Types of outcome measures

Electronic searches

For an outline of the search methods used in the third update of this review see Appendix 1.

For this fourth update we searched the following electronic databases.

• The Cochrane Wounds Group Specialised Register (searched 4th March 2015).

• The Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library 2015, Issue 2).

• Ovid MEDLINE (2012 to 3rd March 2015).

• Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations, 2012 to 3rd March 2015).

• Ovid EMBASE (2012 to 3rd March 2015).

• EBSCO CINAHL (2012 to 4th March 2015).

We searched the Cochrane Central Register of Controlled Trials (CENTRAL) using the following strategy.
#1 MeSH descriptor Surgical Wound Infection explode all trees
#2 MeSH descriptor Surgical Wound Dehiscence explode all trees
#3 MeSH descriptor Infection Control explode all trees
#4 (surg* NEAR/5 infect*):ti,ab,kw
#5 (surg* NEAR/5 wound*):ti,ab,kw
#6 (surg* NEAR/5 site*):ti,ab,kw
#7 (surg* NEAR/5 incision*):ti,ab,kw
#8 (surg* NEAR/5 dehisc*):ti,ab,kw
#9 (wound* NEAR/5 dehisc*):ti,ab,kw
#10 (wound NEAR/5 complication*):ti,ab,kw
#11 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8 OR #9 OR #10)
#12 (plastic NEAR/3 drape*):ti,ab,kw
#13 (adhes* NEAR/3 drape*):ti,ab,kw
#14 (skin NEAR/3 drape*):ti,ab,kw
#15 (incis* NEAR/3 drape*):ti,ab,kw
#16 (iodophor NEAR/3 drape*):ti,ab,kw
#17 (iodine NEAR/3 drape*):ti,ab,kw
#18 (opsite or steridrape or ioban):ti,ab,kw
#19 (#12 OR #13 OR #14 OR #15 OR #16 OR #17 OR #18)
#20 (#11 AND #19)

The search strategies for Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL can be found in Appendix 2, Appendix 3 and Appendix 4 respectively. We combined the Ovid MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity‐ and precision‐maximising version (2008 revision); Ovid format (Lefebvre 2011). We combined the EMBASE search with the Ovid EMBASE filter developed by the UK Cochrane Centre, which is also cited in the Cochrane Handbook (Lefebvre 2011). We combined the CINAHL searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN) (SIGN 2012). We did not apply any date or language restrictions.

Searching other resources

We contacted researchers and manufactures in order to obtain any unpublished data. We also searched reference lists of potentially useful articles.

Selection of studies

For the initial review, two authors (JW, AA) independently assessed the title and abstracts of references identified by the search strategy. We then retrieved full reports of all potentially relevant trials for further assessment of eligibility, based on the inclusion criteria. We settled differences of opinion by consensus or referral to the editorial base of the Wounds Group. There was no blinding of authorship. For this updated review, JW excluded trials and the Managing Editor of the Wounds Group verified their exclusion.

Data extraction and management

Two review authors (JW,AA) independently extracted the following data, using a piloted data extraction sheet: type of study, country, study setting, number of participants, sex, mean age, type of surgery, preoperative wound classification, predisposing risk factors by treatment groups, type of drape, draping procedure, type of preoperative skin preparation, prophylactic or therapeutic antibiotic use, all primary and secondary outcome measures reported and authors' conclusions. Clarification about aspects of the trial were required from all of the authors; five were untraceable (Chiu 1993; Cordtz 1989; Jackson 1971; Psaila 1977; Ward 2001). Additional trial details were received from Dewan 1987 and from the second author of the Segal 2002 trial. We also contacted manufacturers of plastic adhesive drapes (Johnson & Johnson, 3M Company and Smith & Nephew) to request details of any unpublished trials. A representative of each of these manufacturers responded; no current trials are underway and they were unaware of any unpublished trials.

Assessment of risk of bias in included studies

Two review authors independently assessed the quality of eligible trials, using a predefined quality assessment form, based on the assessment criteria outlined below. Disagreements between review authors were again resolved by consensus or referral to the editorial base of the Wounds Group. We contacted investigators of included trials to resolve any ambiguities. Each included study was assessed using the Cochrane Collaboration's tool for assessing risk of bias (Higgins 2011). This tool addresses six specific domains, namely sequence generation, allocation concealment, blinding, incomplete outcome data, selective outcome reporting, and other issues (e.g. extreme baseline imbalance) (see Appendix 5 for details of criteria on which the judgement was based). We assessed blinding and completeness of outcome data for each outcome separately. We completed a risk of bias table for each eligible study. We discussed any disagreement amongst authors to achieve a consensus.

We presented an assessment of risk of bias using a 'Risk of bias' summary figure, which presents all of the judgments in a cross‐tabulation of study by entry. This display of internal validity indicates the weight the reader may give the results of each study.

We defined high quality trials as those receiving a 'low risk of bias' rating for the criterion of allocation concealment (central computerised randomisation service or sealed opaque envelopes), and for blinding of outcome assessment.

Measures of treatment effect

For dichotomous outcomes, we calculated risk ratio (RR) plus 95% confidence intervals (CI). For continuous outcomes we calculated mean difference (MD) plus 95% confidence intervals.

Unit of analysis issues

Individual patients were the analytic units in all trials, so there were no unit of analysis issues.

Dealing with missing data

If there was evidence of missing data, we contacted the study authors to request the information. Where trial authors could not provide missing data, we assessed the risk of bias of the missing data and decided if the missing data were of 'low' or 'high' risk of bias according to our risk of bias criteria (Higgins 2011). Or, if data were considered to be missing at random, we analysed the available information.

Assessment of heterogeneity

We assessed heterogeneity using the Chi² statistic with significance being set at P < 0.10. In addition, we investigated the degree of heterogeneity by calculating the I² statistic (Higgins 2002). If we identified evidence of significant heterogeneity (> 50%), we explored potential sources of heterogeneity and a random‐effects approach to the analysis was undertaken. We conducted a narrative review of eligible studies where statistical synthesis of data from more than one study was not possible or considered not appropriate.

Assessment of reporting biases

We completed a 'Risk of bias' table for each eligible study and present an assessment of risk of bias using a 'Risk of bias' summary figure (Figure 1) which presents the judgements in a cross‐tabulation. This display of internal validity indicates the weight the reader may give to the results of each study.

Data synthesis

We analysed data using Review manager software (RevMan 2011). One review author (JW) entered the data and the other author (AA) cross‐checked the printout against their own data extraction forms. We calculated risk ratios (RRs) and 95% confidence intervals (CIs) for dichotomous outcomes (risk ratio is the risk of infection in the intervention group divided by the risk of infection in the control group; a risk ratio of less than one indicates fewer infections in the intervention or adhesive drape group). We calculated mean differences (MDs) and 95% CIs for continuous outcomes. Where appropriate, we pooled the results of comparable trials using a fixed‐effect model, and we reported the pooled estimate together with its 95% CI.

We included all eligible trials in the initial analysis and carried out preplanned sensitivity analyses to evaluate the effect of trial quality. This was done by excluding trials most susceptible to bias (based on the quality assessment): those with inadequate allocation concealment and uncertain or unblinded outcome assessment.

Subgroup analysis and investigation of heterogeneity

We had planned the following four subgroup analyses.

1. Clean surgery compared with contaminated surgery.

2. Individual compared with cluster allocation.

3. Prophylactic antibiotic compared with no prophylaxis.

4. Hair clipping compared with shaving.

The only subgroup analysis that was possible, based on available data, was of clean compared with contaminated surgery. Nor was it possible to undertake a planned sensitivity analysis based on the type of material the drape was made from due to insufficient detail about the products.

Results of the search

The initial search identified 84 possibly relevant titles, and after screening the titles we considered 18 as potentially useful. Both review authors independently retrieved abstracts or full‐texts and reviewed them against the inclusion criteria. Eleven studies did not meet the inclusion criteria and we excluded them from the review. We excluded two further studies in subsequent updates (Breitner 1986; Swenson 2008). For this fourth update, we identified 49 new trials using the search strategy and follow‐up of reference lists. Only one of these trials was potentially relevant but was later excluded (Falk‐Brynhildsen 2013a), see Characteristics of excluded studies.

Included studies

From the initial search, seven RCTs (Chiu 1993; Cordtz 1989; Dewan 1987; Jackson 1971; Psaila 1977; Segal 2002; Ward 2001) met the inclusion criteria (see Characteristics of included studies). We included these seven trials of 4195 participants in the review, with individual trial sizes ranging between 141 to 1340 participants. Five of the trials compared an adhesive drape with no adhesive drape (Chiu 1993; Cordtz 1989; Jackson 1971; Psaila 1977; Ward 2001) and two compared an iodine‐impregnated adhesive drape with no adhesive drape (Dewan 1987; Segal 2002). One study was a multi‐centre trial (Cordtz 1989); the remaining trials were single centre. An a priori sample size calculation, based on a 50% reduction in the infection rate, was reported in one study (Ward 2001). Segal 2002 reported a sample size calculation based on an analysis of results of a pilot study of 120 patients, the trial was then continued, recruiting a further 64 patients.

Surgical procedures included caesarean section (Cordtz 1989; Ward 2001), general or abdominal surgery (Dewan 1987; Jackson 1971; Psaila 1977), hip surgery (Chiu 1993) and cardiac surgery (Segal 2002). Surgical site infection (SSI) was not defined in one study (Chiu 1993); the Characteristics of included studies table contains details of other definitions used.

Four trials used iodine and alcohol to prepare the operative site (Chiu 1993; Cordtz 1989; Dewan 1987; Jackson 1971); one used Savlon and alcoholic chlorhexidine (Psaila 1977); an iodophor/alcohol water insoluble film was used in the Segal 2002 trial; and in the Ward 2001 trial, skin was swabbed with alcoholic chlorhexidine. In the Cordtz 1989 trial, participants were also randomised to have their wound re‐disinfected prior to wound closure. Jackson 1971 ran a concurrent test of antibiotic spray in random cases.

Prophylactic cephalosporin was given to each patient at anaesthetic induction in the Chiu 1993 trial and all patients in the Ward 2001 trial received 1g of cephazolin when the baby's cord was clamped, unless antibiotics were already being administered for therapy or prophylaxis. Antibiotic use was recorded by Cordtz 1989 and Segal 2002 but not reported by group. No information about antibiotic use was provided by other authors (Dewan 1987; Jackson 1971; Psaila 1977).

Excluded studies

The Characteristics of excluded studies table contains reasons for excluding 14 of these studies. In summary, six were not RCTs (Breitner 1986; Duvvi 2005; Fairclough 1986; Maxwell 1969; Swenson 2008; Yoshimura 2003), three did not report SSI rates (French 1976; Ha'eri 1983; Manncke 1984; Falk‐Brynhildsen 2013a), one did not report the number of participants in each group (Lewis 1984) and an adhesive drape was not used in the remaining three trials (Nystrom 1980; Nystrom 1984; Williams 1972). We excluded one trial from the first review update which was waiting assessment, as it reported colonisation rates but not SSI rates (Breitner 1986).

Random sequence generation

In all trials, the trial authors stated that participants were randomly allocated to the intervention. It was unclear how the allocation sequence was generated in three trials (Chiu 1993; Psaila 1977; Segal 2002). In the Cordtz 1989 trial, the National Centre for Hospital Hygiene was responsible for the randomisation process; Dewan 1987 and Ward 2001 used a random number table and in the Jackson 1971 trial, a 'spin of the coin' was used.

Allocation concealment

Allocation concealment was adequate in three studies. Segal 2002 asked surgeons participating in the trial to draw the treatment allocation from a 'closed sack' at the beginning of surgery and Ward 2001 and Dewan 1987 used sealed envelopes for group allocation. In other studies the information was not available to judge (unclear), although we contacted trial authors where possible (Chiu 1993; Cordtz 1989; Jackson 1971; Psaila 1977).

Blinding

It was impossible for surgeons to be blinded to the intervention. In the Ward 2001 and Dewan 1987 trials, outcomes were assessed by staff who were unaware of group assignment. The study investigators inspected wounds for signs of infection in the Jackson 1971 and Segal 2002 trials. In all other trials it was unclear who was responsible for assessing outcomes, and whether those who did inspect wounds for signs of infection were aware of group assignment (Chiu 1993; Cordtz 1989; Psaila 1977).

Incomplete outcome data

One trial did not indicate the period of follow‐up (Psaila 1977). In the remaining trials, follow‐up ranged between five days and six months (Characteristics of included studies table). In the Dewan 1987 trial, 46 patients (4.2%) were unable to be tracked and were excluded from the analysis. Based on reported data, follow‐up appeared to be complete in all of the other included trials. However, the absence of detailed participant flow charts, or any reference to the number who started the trial and were unable to be followed up, makes assessment of rates difficult, particularly as the follow‐up periods were lengthy in some studies, increasing the likelihood of incomplete follow‐up.

Selective reporting

Results for all expected outcomes were reported in all of the trials.

Other bias

Intention‐to‐treat analysis

None of the trials reported group assignment violations, and so it is difficult to assess whether patient outcomes were analysed in the group to which they were assigned. None of the trials specifically reported that they used an intention‐to‐treat analysis.

Baseline comparability

No information was available about baseline comparability for five trials (Chiu 1993; Cordtz 1989; Jackson 1971; Psaila 1977; Segal 2002). In the Dewan 1987 trial, the author stated that groups were similar for all risk factors but no data was presented. Ward 2001 stated that, apart from age and parity, groups were comparable at baseline but again, no data were available for comparison.

Conflict of interest

No conflict of interests issues were reported by any of the trial authors

for the main comparison

2

Adhesive drapes compared with no adhesive drapes (Analysis: 1)

Iodine‐impregnated adhesive drapes compared with no adhesive drapes (Analysis:2)

Summary

Comment: Hello,

I am sending this message as a representative of the Association of periOperative Registered Nurses (AORN). We have provided a recommendation for our members based on the conclusion of a Cochrane systematic review with meta analysis. The methodology and conclusions of the researchers are being challenged. We would respectfully request a response regarding the questions posed.

AORN is a nonprofit membership association that represents the professional interests of more than 160,000 perioperative nurses by providing nursing education, standards, and clinical practice resources to enable optimal outcomes for patients undergoing operative and other invasive procedures. AORN’s 40,000 registered nurse members manage, teach, and practice perioperative nursing, are enrolled in nursing education, or are engaged in perioperative research.

Each year, AORN publishes its Perioperative Standards and Recommended Practices. AORN’s recommended practices represent what is believed to be optimal and achievable perioperative nursing practice and are based on the highest level of evidence available. The recommended practices describe excellent perioperative nursing practices, promote patient and health care worker safety, and guide policy and procedure development in surgical and invasive procedure settings.

Each recommended practices document focuses on a specific question or topic. The evidence review begins with a systematic literature search conducted using the databases MEDLINE®, CINAHL®, Scopus®, and the Cochrane Database of Systematic Reviews for meta‐analyses, randomized and nonrandomized trials and studies, systematic and nonsystematic reviews, and opinion documents and letters to identify articles related to the topic. The search is conducted by a medical librarian employed by AORN. As relevant studies are located, they are independently evaluated and critically appraised according to the strength and quality of the evidence using the Johns Hopkins Evidence‐Based Practice Model Evidence Appraisal tools, adapted with permission for use in the AORN Authoring System™. The reviewers participate in conference calls to discuss the appraisal scores and to establish consensus. Each article or study is assigned an appraisal score as agreed on by the reviewers. The appraisal scores of individual references are noted in brackets after the citations in the references section of the RP document, as applicable.

After the studies are appraised, the collective evidence supporting each intervention within a specific recommendation is rated using the Oncology Nursing Society Putting Evidence into Practice® schema. Factors considered in review of collective evidence are the quality of research, quantity of similar studies on a given topic, and consistency of results supporting a recommendation.

In our 2013 AORN “Recommended practices for sterile technique,” the following recommendation was made:

• Plastic adhesive incise drapes should not be used.

In a systematic review of seven randomized, controlled studies involving 4,195 patients, researchers concluded there was no evidence to support the use of plastic adhesive incise drapes as a method for reducing infection, and that there was some evidence that infection rates may be increased when adhesive incise drapes are used. A meta‐analysis of five studies included in the review, which included 3,082 participants, compared plain plastic adhesive incise drapes with no drape and showed a significantly higher number of patients developed a surgical site infection when the adhesive incise drape was used. There was no effect on surgical site infection rates according to a meta analysis of two additional studies, including 1,113 participants, which compared iodine impregnated plastic adhesive incise drapes with no drape. The researchers theorized that the patient’s skin is not likely to be a primary cause of surgical site infection if it is properly disinfected, and they concluded that attempting to isolate the skin from the surgical wound is of no benefit and may create increased moisture and bacterial growth under adhesive drapes.

The following evidence was cited to support this recommendation:

Webster J, Alghamdi A. Use of plastic adhesive drapes during surgery for preventing surgical site infection. Cochrane Database Syst Rev. 2011;1.

We are aware that this Cochrane review was updated in 2013, with no new studies identified and the conclusions of the researchers remaining unchanged.

According to our AORN model for individual evidence appraisal, the 2011 systematic review with meta analysis received the highest possible score for quality and strength of evidence, and the collective body of evidence was judged by consensus to be sufficient for qualification as a recommendation for practice.

The AORN recommendation not to use the adhesive incise drapes has received criticism by those who claim that the Cochrane meta analysis was flawed for the following reasons:

1. Clear incise drapes and antimicrobial incise drapes were analyzed separately and have different flaws.
a. All clear incise drapes were included as one entity despite the fact that not all of the products analyzed in the report are available and that the only common feature of clear incise drapes made by different manufacturers is that they are clear. Any differences in performance as a consequence of production history, adhesive, chemistry, etc., were not considered. As a result, those questioning the recommendation believe the conclusion of the researchers that the clear incise drapes raise the risk of surgical site infection is incorrect.
2. The meta analysis on iodine containing drapes failed to isolate those cases where infections are influenced by the use of such a drape, i.e., clean and clean‐contaminated cases from those where the drape is not of clear value, i.e., contaminated or dirty surgery. As a result, those questioning the recommendation believe the conclusion of the researchers is conceptually flawed.
a. Those questioning the recommendation believe the use of antimicrobial impregnated incise drapes is commonly restricted to surgical cases where the nominal surgical site infection rate is approximately 1%; therefore, a randomized controlled trial would require in excess of 40,000 subjects.
3. The Cochrane review contradicts the clinical literature when speculating in the discussion that skin organisms do not cause surgical site infection.
4. The statistical methods used in the antimicrobial portion of the analysis are inconsistent with the Cochrane Collaboration methodology, in that simply combining data and summing results is an inappropriate method for analysis.

AORN would greatly appreciate Cochrane’s review of and response to the criticisms outlined above. We have suggested that these individuals contact Cochrane directly; however, this is not likely to happen. We believe it is important for these questions to be addressed. AORN is dedicated to providing recommendations for perioperative practice that are a credible and indispensable resource to perioperative nurses and other members of the surgical team. The use of scientific evidence to support national recommendations about clinical decisions has become an expectation of perioperative health care professionals. Evidence based practice is an essential method of improving patient care by promoting decisions based on scientific evidence rather than on the opinion of the individual health care provider.

Thank you so much for your swift attention to the issues expressed in this message. We look forward to hearing from you in the near future. Please do not hesitate to call or write if you have any questions or need additional clarification.

I certify that I have no affiliations with or involvement in any organization or entity with a financial interest in the subject matter of my feedback.

Reply

Response by the review author Joan Webster

The limitations of this Cochrane review include:

1. The clinical studies included in the analysis were not powered to detect a reasonable difference in SSI rates. When studies are not powered to detect a difference in an outcome, the result is that even if there were a difference in SSI rate attributable to the adhesive drape, the studies would conclude that there was no difference. Adequate statistical power is critical because a false‐negative result is a predictable consequence including an insufficient number of patients. For example, with a baseline SSI rate of 5% and a reasonable 20% reduction in SSI (to 4%), 18,000 subjects are needed to provide 90% power. Consider the two iodophor‐impregnated drape studies included in the Cochrane review; the minimum reduction of SSI rate required to detect an inter‐group difference given the number of patients actually included is shown in Table 1.

Table 1. Sample Size of Iodophor‐Impregnated Drape Studies

*For clean and clean‐contaminated procedures

Segal et al is thus uninterpretable. Dewan et al would only detect a completely implausible 70% reduction in infection risk; from a practical perspective, it is also uninterpretable.

The same calculations can be made for the other five studies used for clear drapes. For four of the studies the reduction in SSI needed to detect a difference ranged from 45% to 95%, and for one of the studies it was not possible to detect any difference. Thus, none of the clinical studies included in this Cochrane review was powered to detect a reasonable SSI difference.

According to the Evidence Level and Quality Guide in the Johns Hopkins Nursing Evidence‐Based Practice: Model and Guidelines, Second Edition, 2012, Appendix C, these seven studies fall under Level I Evidence (randomized controlled trials or RCT), and a Quality level C “Low Quality or Major Flaws” due to “insufficient sample size for the study design; conclusions cannot be drawn.”

Many individual studies included in Cochrane reviews are under‐powered. The strength of meta analysis is the pooling of trials which individually may be underpowered but together increase statistical power. Moreover, because reviews are updated every 2 years, Cochrane reviews ensure that evidence is cumulative. Cochrane reviewers are committed to scientific rigor and ensuring that reviews are free of any conflicts of interest. Careful peer review, including statistical review, is undertaken before any review is published.

With respect, the authors of the feedback are making the mistake of confusing internal validity with statistical power. These are completely different issues; the former concerns whether the results of the study are likely to be a true reflection of the effect of the intervention on the people in the study (or alternatively whether they reflect a bias in the design or method). Low statistical power does not introduce bias, but it reduces the precision of the estimate, so that one is less likely to detect a real treatment difference (if it exists) as statistically significant.

2. For both meta‐analyses, clear and iodine‐impregnated drapes, the definition of SSI was different among the studies, and the SSI data from all four wound classes was [sic] combined to determine the effect of incise drapes. This is conceptually flawed. There are four wound categories: clean, clean‐contaminated, contaminated and dirty. Skin organisms are the major cause of SSI in clean and clean‐contaminated surgeries ( 1) Mangram A et al. Guideline for the Prevention of Surgical Site Infection, 1999 The Hospital Infection Control Practices Advisory Committee Infect Control Hosp Epidemiol. Vol 20, No. 4, pp 247 ‐ 278 ; and 2) Anderson D., Surgical Site Infections Infec Dis Clin N Am 25 (2011) 135‐153), for which an incise drape may provide benefit by way of reducing microbial contamination of the wound and helping to maintain the sterile field. On the other hand, non‐skin pathogens are the primary cause of SSIs for dirty and contaminated procedures.

The Cochrane review failed to distinguish among types of wound class and, to study the effect of adhesive drapes, pooled all the SSI data from all wound classes, which is conceptually flawed.

This is incorrect. Please see ‘Analysis 1.2and 1.3: Adhesive drapes versus no adhesive drapes’ in the updated review, which shows the surgical site infection rate by wound classification. No benefit of effect for plastic drapes was found in any category. Moreover, inAnalysis 1.1, irrespective of wound category, the SSI rate was not statistically lower in the plastic drape group, in any study.

3. The clear adhesive incise drape meta‐analysis pools SSI data from five studies that used a wide variety of clear incise drapes. There was no distinction among materials, manufacturing processes, adhesives, or important study design factors. For example, two of the studies used linen or cotton drapes which are known to allow fluid and microbial strike‐through, two used drapes that are no longer available, and one remarkably did not even identify the drape used (Table 2). In fact, the only characteristic these clear adhesive incise drapes share is their transparency. Comparability in treatment and outcome are required for valid meta‐analysis — a requirement that was unmet in this case.

Table 2 – Clear Adhesive Incise Drapes

This information is quite irrelevant. In fact, using the statement that: “Linen drapes were used which are known to allow fluid and microbial strike‐through (No barrier function)”, actually provides additional evidence for the failure of incise drapes. That is, plastic drapes could not be shown to be superior, even to these ‘flawed’ linen comparisons.

4. Five studies were included in the meta‐analysis for clear incise drapes. The relative risk of surgical site infections was 1.23 (95% CI 1.02 – 1.48) which is (barely) statistically significant. However, this purported risk traces to Cordtz et al. (1989), in which the authors specify that the rates of infection were “the same in draped patients and control.” The Cochrane Collaboration’s conclusion that adhesive drapes augment infection risk is supported by only a single study — from which even the authors did not conclude that risk was increased.

An important design feature of systematic reviews is the pre‐specification of review methodology, including anticipation of major decisions (such as choice of cut‐point for statistical significance) whilst still “blind” to study results (hence the publication of review protocols). We followed our pre‐specified protocol and its decisions faithfully, our methods are transparent. The authors of the feedback seem to be implying that we should alter our pre‐specified methods if we don't like the findings, or don't agree with the conclusions of individual studies. This would reflect a traditional approach to reviewing that introduces bias and we are keen to avoid it.

The five included trials represent a population of over 3,000 participants. A relative risk of 1.23 indicates a 23% higher risk of infection in the plastic drape group. This is quite an important difference. The review presents the data which speak for themselves; we do avoid (as per Cochrane Collaboration guidance) the use of rather biased and potentially misleading phrases such as “barely statistically significant”; “tending to statistical significance”; “almost statistically significant”. It is not unusual to read a trial report where an author reports that the rates if infection were similar and then when the data presented in the report are analysed there is in fact a statistically significant difference. This is a strength of the independence and rigor of a Cochrane review.

5. Antimicrobial prophylaxis, serum glucose concentration, proper hair removal, and maintaining normothermia are important covariates that impact risk of SSI. In most studies, these issues were not even addressed, much less separately reported.

In randomized controlled trials these factors would be balanced across treatment groups; this is the advantage and strength of randomization.

In addition to these limitations, the authors of this Cochrane report conclude that: “a large, high

quality definite [sic] RCT may be warranted to determine whether modern adhesive drapes do prevent or reduce SSIs”. Thus, even the Cochrane authors recognize that their conclusions are weak and do not constitute sufficient evidence to support a practice recommendation.

Our conclusion (that further research is needed) reflects the fact that the research in this field has shortcomings in volume and quality. However our conclusion that the available evidence does not suggest that plastic adhesive drapes reduce SSI rates still

Contributors

Sharon A. Van Wicklin, Perioperative Nursing Specialist, AORN (Association of periOperative Registered Nurses)
Joan Webster, Nursing Director, Research. Centre for Clinical Nursing. Royal Brisbane and Women's Hospital. Brisbane, Queensland

Summary

Comment: It is the view of 3M that the Cochrane Review titled Use of plastic adhesive incise drapes for preventing surgical site infection published in 2007 and subsequently have been issued as meta‐analysis. Since it was issued, the review should have critically highlighted the many shortcomings of the data, the absence of meaningful information, and the inability to determine the effect of incise drapes on surgical site infection rates. This Cochrane Review has recently had a significant impact on product use recommendations in the USA which may have far‐reaching repercussions so 3M feels compelled to provide feedback at this time.
3M has involved external experts (surgeons, biostatisticians, epidemiologists) to review the Cochrane Report and the seven clinical studies included and to provide honest, objective comments. Their consensus is that this Cochrane Review included studies that are flawed in many ways, making it unhelpful for policy.
The key flaws can be summarized as follows:
1. Failure in all studies to control for confounding
2. Likelihood of bias
3. Absence of power estimates, and thus, potential for type II errors
4. Heterogeneity of the study populations, definition of primary endpoint (infections) and incise drapes that seem to preclude a meta‐analysis
5. The broad time span of the studies included and the absence of data on over a decade make the conclusions unuseful for the current medical practice

3M does acknowledge that there is a compelling need to conduct further clinical studies to demonstrate the effect of plastic adhesive incise drapes on surgical site infection.
Since we could not find a way to attach a document in this feedback page, 3M respectfully requests the Cochrane Organization to provide a mechanism, i.e. an e‐mail address, to submit a document that includes a detailed scientific review.
We appreciate in advance your attention to this matter and we look forward to hearing from your soon.

I have modified the conflict of interest statement below to declare my interests:
These comments are being provided on behalf of 3M, a manufacturer of plastic adhesive incise drapes (with and without an antimicrobial agent) the subject of this Cochrane

It was not possible to include a copy of this report in this section of the review but a copy can be obtained from the Cochrane Wounds Group editorial base.

Reply

Response by the Statistical Editor of the Cochrane Wounds Group

With respect to the comments from 3 M:

I don't think the Cochrane review is flawed, it followed the recommended methods. It is the studies contained within the review which are flawed, not the actual review. None of their 5 main points refer to the review methods, they all relate to either the methods of the studies or the evidence as a whole (in terms of heterogeneity and the wide time span).

1. Confounding: this isn't a problem. The review only included randomised controlled trials, as these have been randomised all known and unknown confounders should be balanced between the groups. There is no need to perform any matching, stratified or multivariate analysis. Matching would be inappropriate as is not relevant to an RCT, only observational studies. The other analysis methods could be used, for example, to adjust for centre if the randomisation was stratified by centre, or to account for prognostic factors, maybe type of surgery. But they are not strictly necessary.

2. Bias: I am not clear what is meant by the first point which compared the earlier to the later studies. Both sets of studies are quite likely to contain the same flaws, and again confounding is not an issue. Failure to report the randomisation method and lack of blinding, yes, this is a problem with the studies. Lack of randomisation details is a common problem with reviews but it is not really a form of bias just poor reporting. For the blinding, due to the intervention they couldn't blind the surgeons. But could blind the outcome assessor. The review comments on this in the risk of bias assessment and only 2 trials had blinded outcome assessment. The conclusion in the abstract says that further trials are needed using blinded outcome assessment so I think this has been addressed in the review.

3. Type II errors. True this is a fair comment. This could have been commented on in the review but it wasn't. However the risk of bias tool used doesn't judge whether or not there was a sample size calculation, so it was not discussed in the risk of bias section. But this is a flaw with the studies, and it is a common one. I read a lot of papers and it is the minority which report a sample size calculation.

4. Heterogeneity. Type of surgery and wound class, yes, these are possible causes of heterogeneity and could have been included as subgroup analyses. The review states the planned subgroup analyses (although not necessarily performed due to a lack of data) and one of them was clean compared with contaminated surgery. This has been done, there are forest plots showing results grouped by wound classification. Type of surgery has not been looked at but the thing to note here is that the potential sources of heterogeneity / subgroup analyses should be prespecified in the protocol, and not just explored within the review (as the more subgroup analyses you do the more likely you are to find something). So as surgery type was not prespecified it must not have been thought to be a potential factor. Definition of infection, yes this varied, but that is what the studies reported so the review has to use what the studies say. However the question this review is addressing is the use of adhesive drapes versus not, to address the actual type of drape was not part of the question or the protocol. Which is why it hasn't been done (and one study didn't tell you anyway).

5. Broad time span. Yes this is a good point. It is a wide time frame and presumably things have changed quite a lot since 1971. This could have been discussed more by the review. They do cover it briefly in terms of the changes in the product over 30 years but the points about antibiotic resistance of organisms could be added. It might also be useful to do a sensitivity analysis removing the 2 oldest studies to see how it changes the results.

Additional comments:

· Lack of reporting of bacteria and MRSA, single institutions, all fair comment.
· Increase in SSI, the results of analysis 1.1 do show this. Three of the five studies do show more SSI with the drapes although not statistically significant in 2 of them.

Conclusions.

The meta‐analyses are not flawed. Some of the included studies were at moderate risk of bias, some were unclear for many aspects. This is covered by the discussion of the review. The review can only really discuss those aspects assessed by the risk of bias tool. It does highlight shortcomings in the evidence but aspects such as the power of the studies, and the materials and manufacturing processes of the drapes were outside the review's scope and not part of the protocol which is why they haven't been addressed.

Comments by Professor J. Martin Bland, Professor of Health Statistics

The critique raises five points:

1. Failure in all studies to control for confounding.

2. Likelihood of bias.

3. Absence of power estimates and thus the potential for type II errors.

4. Heterogeneity of the study populations, definition of primary endpoint (infections) and incise drapes that seem to preclude a meta‐analysis.

5. The broad time span of the studies included and the absence of data in over a decade make the conclusions not useful for current medical practices.

1. Failure in all studies to control for confounding.

“Confounding” occurs when the outcome variable, infection, and the explanatory variable, drapes, are both related to a third, pre‐existing variable which affects the apparent relationship between them. Confounding should not occur in a randomised trial, because the randomised groups are from the same population. They should not differ in any way other than those arising by chance. The critics say:

“In no study was there matching on the front end, a stratified analysis on the back end or a multivariate analysis. Examples of such confounding variables include age, co‐morbidities, obesity, serum glucose concentration, proper hair removal, normothermia, and receipt of antibiotics preoperatively and their timing relative to incisions. All of these important covariates impact the risk of SSI.”

If there are covariates which are prognostic, related to the outcome variable, it is a good idea to adjust for them. This will improve the precision of estimates. This can only be done using the participant level data, so should be done by the original investigators. It is a feature of clinical trials that most of them could have been done better. If all trials were done to the highest standard, we would not need systematic reviews, but the world is not like that. The effect of not adjusting is to widen confidence intervals and increase P values. It does not invalidate or bias the trial; it makes it inefficient.

2. Likelihood of bias.

The critics say:

“If the initial 4 studies performed between 1971 and 1989 (3480 subjects), versus those from 1993 to 2001 (826 subjects), had errors (confounding issues or bias) in favor of no efficacy, bias would be likely.”

There is no doubt that this is a true statement. This true statement does not imply that there is, in fact, any bias. As noted above, there should not be confounding in a randomised trial and failure to adjust for covariates does not produce bias. The critics also say:

“The failure to provide a recorded randomization method and the lack of blinding are both well known to lead to bias.”

It is true that both of these are potential sources of bias. They do not necessarily lead to bias. General experience is that biases are usually in favour of the test treatment.

3. Absence of power estimates and thus the potential for type II errors.

The critics say:

“All seven studies in the meta‐analyses were grossly underpowered and thus the ability to find a difference – if one existed – is negated, even in the meta analysis. None of the seven clinical studies included in the analyses were powered to detect a reasonable difference in SSI rates. Adequate statistical power is critical because a false‐negative result is a predictable consequence of including an insufficient number of patients. For example, with a baseline SSI rate of 5% and a reasonable 20% reduction in SSI (to 4%), 18,000 subjects are needed to provide 90% power.”

This calculation is correct. Many, if not most, randomised clinical trials are underpowered. However, when the trials have been carried out, we should not refuse to analyse them on these grounds. Systematic review was introduced to deal with just this problem and enables us to get the maximum amount of information from the inadequate data available. Confidence intervals, the preferred method to report results from trial, do not give us a yes or no answer but a range of plausible values for the treatment effect. In this review, for adhesive drapes the risk of SSI is estimated to be between 1.02 and 1.48 times the risk without adhesive drapes, which does not include the critics’ postulated 0.80, and for iodine impregnated adhesive drapes the risk of SSI is estimated to be between 0.66 and 1.60 times the risk without adhesive drapes, which does include the critics’ postulated 0.80. Thus we have good evidence that adhesive drapes increase the risk of infection, though possibly only by as much as 3%, and that iodine impregnated adhesive drapes may reduce the risk of SSI by up to a third and may increase it by up to two‐thirds.

Significance test approaches are not as informative. The fact that a particular study could not produce a significant difference alone does not mean it is not informative and interpretable in a meta‐analysis.

4. Heterogeneity of the study populations, definition of primary endpoint (infections) and incise drapes that seem to preclude a meta‐analysis.

There is certainly clinical heterogeneity between these studies. It may be that adhesive drapes work completely differently in different surgical procedures and using different wounds definitions, to the extent that an average effect is of no interest. If that is true, we would need very large trials separately for each type of surgery and each definition of infection. Is it plausible that the effect of adhesive drapes varies so much? This would make it very difficult to know when they could be used, in the absence of these trials. But surely while we wait for them we should make the best use of what data are currently available.

We could note that there is no evidence of statistical heterogeneity in SSI relative risk, though the clinical heterogeneity would certainly lead me to prefer a random effects model to be used. Using current methods, and the random effects and the fixed effect analyses will be identical. There is no statistical reason to suppose that the clinical heterogeneity produces heterogeneity of effects.

5. The broad time span of the studies included and the absence of data in over a decade make the conclusions not useful for current medical practices.

The authors say:

“The first study was performed 41 years ago and the last 31 years afterwards, and no studies were included for the last 11 years. This is problematic. The practices of medicine and surgery have changed greatly; infection control and quality of care have become more visible and more effective over the time span; standardized surveillance is more commonplace now. The fact that there are no studies in over a decade during which time safety has emerged as a priority and guidelines have become more common and are more detailed suggest little relevance to practice today. Furthermore, the organisms causing infections have changed over 41 years and become more antibiotic resistant, prompting some changes in perioperative prophylaxis.”

While this is true, should we need to keep randomising people to treatments where there has been past evidence of harm, in case things have changed? We can only analyse the data available and if we have a system where established effective treatments have to be continually retrialled, things will grind to a halt.

Additional Comments

The critics say: “There was failure to show the spectrum of bacteria implicated in 6/7 studies. In the Chiu study with 14 SSIs, 8 were caused by MRSA (perioperative prophylaxis with an ineffective “cephalosporin”), suggesting a true problem at the hospital, such as an outbreak, and opportunity for co‐founding in the study.”
The point that the spectrum of bacteria implicated might have been informative is a valid one, but there is nothing that reviewers can do about this.

The critics say: “Six of the seven studies were performed in a single institution making generalization problematic.”
By looking at the studies combined, a greater variety of settings is studied, which is a strength of systematic review. This point is nonsensical.

The critics say: “The Cochrane Review authors concluded was that there was some evidence that plastic adhesive incise drapes increase infection rates, but there is no such evidence. Five studies were included in the meta‐analysis for clear incise drapes. The relative risk of surgical site infections was 1.23 (95% CI 1.02 – 1.48) which is (barely) statistically significant. However, this purported risk traces to Cordtz et al. (1989), in which the authors specify that the rates of infection were “the same in draped patients and control.” The Cochrane Collaboration’s conclusion that adhesive drapes augment infection risk is supported by only a single study — from which even the authors did not conclude that risk was increased.”
The confidence interval would certainly convince me that the evidence is that adhesive drapes do not reduce infection. It does not depend on one study alone; four of the five studies have a point estimate of the relative risk greater than 1.00 and the fifth is the smallest study in terms of numbers randomised. That Cordtz et al. choose to interpret “not significant” as “the same” is not the fault of reviewers. This is a very common misunderstanding among clinical researchers.

Response by the review author Joan Webster

OBJECTIVE
The objective of this review is to evaluate the limitations of the Cochrane Review titled “Use of plastic adhesive drapes during surgery for preventing surgical site infection”.

REVIEW
The Cochrane review consisted of two meta‐analyses that assessed the effect of adhesive incise drapes on surgical site infection (SSI) rates:

1. Five trials with the use of clear adhesive incise drapes (non‐antimicrobial)

2. Two trials with the use of iodine‐impregnated adhesive incise drapes.

This Cochrane review is flawed in many ways and the key limitations are summarized below and are also presented in tabular form in the Appendix.

1. Failure in all studies to control for confounding.

2. Likelihood of bias.

3. Absence of power estimates and thus the potential for type II errors.

4. Heterogeneity of the study populations, definition of primary endpoint (infections) and incise drapes that seem to preclude a meta‐analysis.

5. The broad time span of the studies included and the absence of data in over a decade make the conclusions not useful for current medical practices.

1. Confounding. In no study was there matching on the front end, a stratified analysis on the back end or a multivariate analysis. Examples of such confounding variables include age, co‐morbidities, obesity, serum glucose concentration, proper hair removal, normothermia, and receipt of antibiotics preoperatively and their timing relative to incisions. All of these important covariates impact the risk of SSI.
We agree that certain risk factors will impact on an individuals’ risk of acquiring a SSI. However, this Cochrane review only included RCTs, which by definition do not experience confounding (if randomisation is properly conducted – hence the importance of Risk of Bias Assessment).
In the current review, no baseline data were reported for the studies of Cordez (1989), Jackson (1971) or Psaila (1977). Whereas Chiu (1993), Dewan (1987), Segal (2002) and Ward (2001) all indicated that patients were matched for all relevant risk factors at baseline.

2. Bias.

• If the initial 4 studies performed between 1971 and 1989 (3480 subjects), versus those from 1993 to 2001 (826 subjects), had errors (confounding issues or bias) in favor of no efficacy, bias would be likely.

• The failure to provide a recorded randomization method and the lack of blinding are both well known to lead to bias.

Please see above. All studies are assessed for their individual risk of bias in six domains (sequence generation, allocation concealment, blinding, completeness of outcome data, selective reporting, and other biases, such as baseline imbalance). In the table ‘Characteristics of included studies’, shortcomings of each trial are reported against each of these criteria. Many trial reports, published before the CONSORT statement, failed to provide sufficient information to be able to judge the quality of the trials’ conduct. Because of this, it is unclear, in many studies, if bias existed or not. It may have been the case that some requirements outlined in the CONSORT Statement may have been met but simply was not reported.

3. Type II errors. All seven studies in the meta‐analyses were grossly underpowered and thus the ability to find a difference – if one existed – is negated, even in the meta‐analysis.
We agree with the feedback that the studies are underpowered, but they still contain information; the value of which is enhanced by meta‐analysis (by increasing the power). The implied alternative is that we ignore all studies that were individually underpowered or had design flaws. That would consign most of all the medical research ever conducted to the waste bin.

Moreover, because reviews are updated every 2 years, Cochrane reviews ensure that evidence is cumulative. Cochrane reviewers are committed to scientific rigor and ensuring that reviews are free of any conflicts of interest. Careful peer review, including statistical review, is undertaken before any review is published.

4. Heterogeneity. Besides leading to confounding and bias, this aspect of the report usually precludes a meta‐analysis. The most obvious issues include:

· Types of surgery: abdominal – general (N=3), cardiac (N=1), C‐section (N=2), and hip surgery (N=1).
There was no statistical heterogeneity between studies (I² = 0%). In addition, all of the studies trended towards favouring the ‘no drape’ group (with the exception of the smallest study (Psaila 1977)

· Wound Class. The SSI data from all four wound classes were combined to determine the effect of incise drapes. This is conceptually flawed. There are four wound categories: clean, clean‐contaminated, contaminated and dirty. Skin organisms are the major cause of SSI in clean and clean‐contaminated surgeries (1, 2), for which an incise drape may provide benefit by way of reducing microbial contamination of the wound and helping to maintain the sterile field. On the other hand, non‐skin pathogens are the primary cause of SSIs for dirty and contaminated procedures. The Cochrane review failed to distinguish among types of wound class and, to study the effect of adhesive drapes, pooled all the SSI data from all wound classes, which is conceptually flawed. This is incorrect. Please see ‘Analysis 1.2and 1.3: Adhesive drapes versus no adhesive drapes’ in the updated review, which shows the surgical site infection rate by wound classification. No benefit of effect for plastic drapes was found in any category. Moreover, inAnalysis 1.1, irrespective of wound category, the SSI rate was not statistically lower in the plastic drape group, in any study.

Definition of Infection. The inconsistency of definitions for an infection is remarkable from very nonspecific definitions such as “tenderness” to a vague definition of “clinical evidence” to a more robust definition of “pus” – the single definition in two studies. As definitions of infections frequently vary between studies (and sometimes are absent) our inclusion criteria clearly stated that: “For the purposes of this review we accepted the definition of SSI used in the trial”. This is a pragmatic, and we feel entirely defensible, approach.

Clear Incise Drape Used. The clear adhesive incise drape meta‐analysis pools SSI data from five studies that used a wide variety of clear incise drapes. There was no distinction among materials, manufacturing processes, adhesives, or important study design factors. For example, two of the studies used drapes that are no longer available, two of the studies used additionally linen or cotton drapes which are known to allow fluid and microbial strike‐through, and one, remarkably, did not even identify the drape used (Table 2). In fact, the only characteristic these clear adhesive incise drapes share is their transparency. Comparability in treatment and outcome are required for valid meta‐analysis — a requirement that was unmet in this case. This information is quite irrelevant. In fact, using the statement that: “Linen drapes were used which are known to allow fluid and microbial strike‐through (No barrier function)”, actually provides additional evidence for the failure of incise drapes. That is, plastic drapes could not be shown to be superior, even to these ‘flawed’ linen comparisons.

5. Broad time span. The first study was performed 41 years ago and the last 31 years afterwards, and no studies were included for the last 11 years. This is problematic. The practices of medicine and surgery have changed greatly; infection control and quality of care have become more visible and more effective over the time span; standardized surveillance is more commonplace now. The fact that there are no studies in over a decade during which time safety has emerged as a priority and guidelines have become more common and are more detailed suggest little relevance to practice today. Furthermore, the organisms causing infections have changed over 41 years and become more antibiotic resistant, prompting some changes in perioperative prophylaxis. Despite the time span, head to head comparisons between no adhesive plastic drape versus use of an adhesive plastic drape have consistently shown no advantage associated with adhesive drapes. We would be pleased to include information from independent clinical trials in any future update, Cochrane reviews are updated on average every two years but will be updated earlier in the light of substantial new evidence becoming available.

Additional Comments

There was failure to show the spectrum of bacteria implicated in 6/7 studies. In the Chiu study with 14 SSIs, 8 were caused by MRSA (perioperative prophylaxis with an ineffective “cephalosporin”), suggesting a true problem at the hospital, such as an outbreak, and opportunity for co‐founding in the study.This observation is irrelevant; the same conditions existed for both arms of the trial.

Six of the seven studies were performed in a single institution making generalization problematic. Single‐centre trials are not unusual, hence the usefulness of systematic reviews.

The Cochrane Review authors concluded was that there was some evidence that plastic adhesive incise drapes increase infection rates, but there is no such evidence. Five studies were included in the meta‐analysis for clear incise drapes. The relative risk of surgical site infections was 1.23 (95% CI 1.02 – 1.48) which is (barely) statistically significant. However, this purported risk traces to Cordtz et al. (1989), in which the authors specify that the rates of infection were “the same in draped patients and control.” The Cochrane Collaboration’s conclusion that adhesive drapes augment infection risk is supported by only a single study — from which even the authors did not conclude that risk was increased. Again, this is why systematic reviews are so useful, results from one trial are often inconclusive and trial authors can make statements which are not always supported by the data they present. Cochrane review authors are independent, they have no conflicts of interest and present the data and draw conclusions independently of any affiliations. In addition, a statistically significant 23% increase in risk of SSI in the plastic drape group seems to us to be clinically important and ignoring it would be indefensible.

CONCLUSIONS

The meta‐analyses by Webster and Alghandi as published in the Cochrane Review is flawed and should not have been accepted. It fails to critically highlight the many shortcomings for the data, the absence of meaningful information, and the inability to determine the effect of incise drapes on surgical site infection rates.

We do not agree with the assessment of the reviewers from 3M. The review was carefully peer refereed and we are confident in its results.

There is a compelling need to conduct further clinical studies to determine the effect of plastic adhesive incise drapes on surgical site infection rates.

We would be pleased to see published, independent, robust RCTs of plastic adhesive drapes to add to our review in future updates.

Contributors

Nancy Klinger, Manager, Clinical Affairs, 3M Infection Prevention Division (plus the authors of the Technical report)
Gill Worthy, Statistical Editor, Cochrane Wounds Group.
Martin Bland Professor of Health Statistics, University of York.
Joan Webster, Nursing Director, Research. Centre for Clinical Nursing. Royal Brisbane and Women's Hospital. Brisbane, Queensland

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Appendix 1. Search strategy for the third review update ‐ 2012

For this third update we modified the search strategy and ran it over all available years in the following electronic databases.

• The Cochrane Wounds Group Specialised Register (searched 19 July, 2012).

• The Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library 2012, Issue 7).

• Ovid MEDLINE (1946 to July Week 2 2012).

• Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations, July 18, 2012).

• Ovid EMBASE (1974 to Week 28, 2012).

• EBSCO CINAHL (1982 to July 6, 2012).

We searched The Cochrane Central Register of Controlled Trials (CENTRAL) using the following strategy.
#1 MeSH descriptor Surgical Wound Infection explode all trees
#2 MeSH descriptor Surgical Wound Dehiscence explode all trees
#3 MeSH descriptor Infection Control explode all trees
#4 surg* NEAR/5 infection*
#5 surg* NEAR/5 wound*
#6 wound* NEAR/5 infection*
#7 (postoperative or post‐operative) NEAR/5 infection*
#8 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7)
#9 plastic NEAR/3 drape*:ti,ab,kw
#10 adhes* NEAR/3 drape*:ti,ab,kw
#11 skin NEAR/3 drape*:ti,ab,kw
#12 incis* NEAR/3 drape*:ti,ab,kw
#13 iodophor NEAR/3 drape*:ti,ab,kw
#14 iodine NEAR/3 drape*:ti,ab,kw
#15opsite or steridrape or ioban:ti,ab,kw
#16(#9 OR #10 OR #11 OR #12 OR #13 OR #14 OR #15)
#17(#8 AND #16)

The search strategies for Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL can be found in Appendix 2, Appendix 3 and Appendix 4 respectively. We combined the Ovid MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity‐ and precision‐maximising version (2008 revision); Ovid format. We combined the EMBASE and CINAHL searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN). We did not apply any date or language restrictions.

Appendix 2. Ovid MEDLINE search strategy

1 exp Surgical Wound Infection/
2 exp Surgical Wound Dehiscence/
3 exp Infection Control/
4 (surg* adj5 infection*).tw.
5 (surg* adj5 wound*).tw.
6 (surg* adj5 site*).tw.
7 (surg* adj5 incision*).tw.
8 (surg* adj5 dehisc*).tw.
9 (wound* adj5 dehisc*).tw.
10 wound complication*.tw.
11 or/1‐10
12 (plastic adj3 drape*).tw.
13 (adhes* adj3 drape*).tw.
14 (skin adj3 drape*).tw.
15 (incis* adj3 drape*).tw.
16 (iodophor adj3 drape*).tw.
17 (iodine adj3 drape*).tw.
18 (opsite or steridrape or ioban).tw.
19 or/12‐18
20 11 and 19

Appendix 3. Ovid EMBASE search strategy

1 exp Surgical Wound Infection/
2 exp Surgical Wound Dehiscence/
3 exp Infection Control/
4 (surg* adj5 infection*).tw.
5 (surg* adj5 wound*).tw.
6 (surg* adj5 site*).tw.
7 (surg* adj5 incision*).tw.
8 (surg* adj5 dehisc*).tw.
9 (wound* adj5 dehisc*).tw.
10 wound complication*.tw.
11 or/1‐10
12 (plastic adj3 drape*).tw.
13 (adhes* adj3 drape*).tw.
14 (skin adj3 drape*).tw.
15 (incis* adj3 drape*).tw.
16 (iodophor adj3 drape*).tw.
17 (iodine adj3 drape*).tw.
18 (opsite or steridrape or ioban).tw.
19 or/12‐18
20 11 and 19

Appendix 4. EBSCO CINAHL search strategy

S20 S11 and S20
S19 S12 or S13 or S14 or S15 or S16 or S17 or S18 or S19
S18 TI (opsite or steridrape or ioban) or AB (opsite or steridrape or ioban)
S17 TI iodine N3 drape* or AB iodine N3 drape*
S16 TI iodophor* N3 drape* or AB iodophor* N3 drape*
S15 TI incis* N3 drape* or AB incis* N3 drape*
S14 TI skin N3 drape* or AB skin N3 drape*
S13 TI adhes* N3 drape* or AB adhes* N3 drape*
S12 TI plastic N3 drape* or AB plastic N3 drape*
S11 S1 or S2 or S3 or S4 or S5 or S6 or S7 or S8 or S9 or S10
S10 TI wound complication* or AB wound complication*
S9 TI wound* N5 dehisc* or AB wound* N5 dehisc*
S8 TI surg* N5 dehisc* or AB surg* N5 dehisc*
S7 TI surg* N5 incision* or AB surg* N5 incision*
S6 TI surg* N5 site* or AB surg* N5 site*
S5 TI surg* N5 wound* or AB surg* N5 wound*
S4 TI surg* N5 infection* or AB surg* N5 infection*
S3 (MH "Infection Control+")
S2 (MH "Surgical Wound Dehiscence")
S1 (MH "Surgical Wound Infection")

Appendix 5. Risk of bias assessment definitions

Adhesive drapes versus no adhesive drapes

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Iodine‐impregnated adhesive drapes versus no adhesive drapes

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