fiscal cost for each contagion prevented ( number needed to treat for an extra beneficial consequence ( NNTB ) ). We planned to make this calculation by using the NNTB to calculate the fiscal cost of prescribing topical preventive antibiotics to a phone number of patients in order to prevent a single hoist infection. proportion of patients with any relevant adverse effect within 30 days of the operation, i.e. allergic contact dermatitis, anaphylaxis, or infections with patterns of antibiotic resistance. SSI, as defined by the CDC definition of SSI. In this definition infection must occur within 30 days of the routine, consequently this time target was used as a cut‐off for this elementary consequence measure. We besides accepted the trial authors ‘ definitions of contagion. We did not consider outcomes to be eligibility criteria. We considered secondary outcomes with and without validated scales.

The intervention was topical antibiotics in the form of ointments, creams, lotions, solutions, gels, tinctures, foams, pastes, powders and impregnate dressings. We excluded silver medal and antiseptics from our definition of topical antibiotics. We required the topical antibiotic to have been applied after the wound was closed by primary purpose, therefore we excluded antibiotic irrigation and washouts, hypodermic infiltration of antibiotics and any topical discussion applied entirely prior to closure of the scent. We besides excluded studies of antibiotic‐coated sutures. We primitively planned to exclude studies where patients received accompaniment systemic antibiotics, however these studies were included. We included single application postoperatively, or multiple applications in the postoperative period. We recorded dose of antibiotic if this data was available. The topical antibiotic may have been applied with or without a dressing. The comparison group was placebo ‐ which could have contained the fomite of the topical antibiotic ‐ oral antibiotic, option topical antibiotic, topical antiseptic or no treatment. We did not consider the comparator groups to be homogeneous for the purposes of data synthesis. instances where there had been antibiotic irrigation or washout of wounds, hypodermic percolation of the antibiotic, or any topical treatment applied alone prior to wound closure ( not after ). studies involving people with wounds that were already infected ( secondarily infected wounds ), i.e. we did not include antibiotics for treating ‐ rather than preventing ‐ hoist infection ; studies involving blend populations ( if the data allowed the results from the relevant population to be extracted ). Our definition of mix populations for the function of this recapitulation was a trial in which some of the participants fulfilled the inclusion criteria and others did not. people of any historic period, sex or country of origin who had undergo surgical procedures where bring around of the surgical injure was planned by elementary purpose, i.e. where wounds had edges approximated with sutures, staples, clips or glue ; We included randomized controlled trials ( RCTs ) and quasi‐randomized controlled trials ( quasi‐RCTs ) with a parallel group plan. Quasi‐RCTs are trials which use a quasi‐random allotment strategy, such as surrogate days, date of birth, or hospital numeral. We included trials published as abstracts if sufficient data were available. We besides included unpublished RCTs if sufficient data were available. We accepted trials with opposite designs ( one injure treated with topical antibiotic, and the early treated without topical antibiotic, at unlike sites in the lapp patient ). We searched the bibliographies of all retrieved and relevant publications identified by the database searches for extra eligible trials. We contacted manufacturers and pharmaceutical companies regarding studies for inclusion. The search strategies used for CENTRAL, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL can be found in Appendix 1. We combined the Ovid MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomize trials in MEDLINE : sensitivity‐ and precision‐maximising version ( 2008 revision ) ( Lefebvre 2011 ). We combined the Embase search with the Ovid Embase percolate developed by the UK Cochrane Centre ( Lefebvre 2011 ). We combined the CINAHL searches with the trial filters developed by the scottish Intercollegiate Guidelines Network ( SIGN 2015 ). We did not restrict studies with deference to speech, date of publication or survey set. The research was first conducted in May 2015. The search was repeated in May 2016 to ensure currency of include studies .

Data collection and analysis

We followed guidelines given by the Cochrane Handbook for Systematic Reviews of Intervention s ( Deeks 2011 ), and Cochrane Wounds.

Selection of studies

Two review authors ( CH and JB ) independently screened the studies identified by the literature search. These review authors analyzed the titles and abstracts of all citations found through the search strategy described above. They obtained a transcript of the full article for each citation reporting a potentially eligible trial. independently, the two review authors applied the eligibility criteria ; any discrepancies were resolved by consensus discussion with the third base revue author ( MVD ). Where necessary and possible, extra information was sought from the principal investigator of the trial refer. We justified, in the final report, any excommunication of a potentially eligible trial from the follow-up. We completed a PRISMA flow chart to summarize this process ( Figure 1 ) ( Liberati 2009 ).

  • Open in figure viewer
  • figure 1 Study flow diagram Study flow diagram

    Data extraction and management

    Two review authors ( CH and PL ) independently extracted data. We summarised data using a pre designed data origin form. We piloted the data origin creature before use. Data from trials published in double were included lone once. Any discrepancy was resolved by discussion or in reference with a one-third follow-up writer ( MVD ). We extracted the follow data :

    • source ( study ID ) ;
    • eligibility ( confirm eligibility for review ) ;
    • characteristics of the trial ( date of cogitation, setting, placement of care, state, source of fund ) ;
    • methods ( study design, sequence genesis, allocation sequence screen, blind, other concerns about bias ) ;
    • participants ( act, diagnostic criteria, age, sexual activity, comorbidities, class of wind ) ;
    • treatment ( type of topical antibiotic, delivery vehicle, dose, frequency of application, cobalt interventions ) ;
    • relative interposition ( placebo cream, alternative antibiotic cream, no treatment dominance ) ;
    • for each consequence of interest : consequence definition, unit of measurement, upper and lower limits for scales ;
    • primary outcomes ( definition of SSI, unit of measurement ) ;
    • secondary outcomes ( result definition and unit of measurement ) ;
    • results ( count of participants allocated to each intervention group, sample size, missing participants, summary data ‐ e.g. 2×2 data for dichotomous data, means and standard deviations for continuous data, appraisal of effect with confidence intervals and P value, subgroup psychoanalysis ).
    • key conclusions of survey authors.

    Assessment of risk of bias in included studies

    Two reappraisal authors ( CH and PL ) independently assessed each included discipline. Assessment was undertaken using the Cochrane creature for assessing risk of bias ( Higgins 2011 ). The ‘Risk of bias ‘ instrument considers the domains of :

    We acknowledge that there is no accept definition of what constitutes a test at eminent risk of bias, therefore we set a threshold so that trials that we assessed as being at hazard for any one of the follow essential elements of gamble of bias ‐ sequence generation, allotment screen and tax assessor blinding ‐ we considered to be at high risk of bias. besides, if miss consequence data were unevenly distributed over the intervention arms, we discussed this, considered the study at high risk of abrasion bias, and considered performing intention‐to‐treat ( ITT ) analysis. We completed a ‘Risk of bias ‘ table for each eligible study. We combined these data into a ‘Risk of bias ‘ drumhead figure.

    Measures of treatment effect

    The primary consequence was dichotomous ( SSI or no SSI ) and was measured using risk ratio as the effect measure, with 95 % confidence interval. We planned to use base remainder with standard deviation and 95 % confidence time interval to analyse continuous variables ( patient satisfaction ) using the same scales. Where different scales were used to assess continuous outcomes, we planned to use exchangeable mean difference with standard deviation in the analysis ( Deeks 2011 ). Time‐to‐healing is a form of time‐to‐event data, more correctly analyzed using survival methods which can account for censoring ( i.e. barely for the time that people were observed, so it takes account of when they dropped out ) ; it would have been inappropriate to report and analyse time‐to‐wound bring around as if it were a continuous variable unless everyone healed and there was no loss to follow‐up. In practice there were no continuous variables in our review, and time‐to‐event data were not available for analysis in a available format.

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    Unit of analysis issues

    The unit of analysis in trials was most likely to be the patient recruited into the test. It was possible that cluster‐randomized trial designs would be encountered, for exemplar randomization by surgeon, or by operating list, or by general practice operating room or hospital. We planned to analyse such trials based on allotment, using compendious values for each cluster, allowing the clusters to become the individuals and analyse them as such. We planned to use analysis from the trials that adjusted for cluster. Where trials did not adjust for clustering, we planned to attempt adjust the analysis for correlation coefficient. This can be done through a act of methods, ideally based on a direct estimate of the necessitate effect bill as stated in Deeks 2011. We planned to use the generic inverse discrepancy method acting in Review Manager 5 ( RevMan 2014 ) to pool data from bunch randomized trials ( Deeks 2011 ). In commit, there were no cluster‐randomized trials encountered in our reappraisal. If there were three arms in a survey, where two of the arms were clinically alike, for the purposes of the review, we combined them to create a single pair‐wise comparison. Where we could not combine arms and we included multiple arms in the lapp analysis, we planned to divide the control group ( s ) between the two arms for the purpose of comparison. In arrange to avoid unit of analysis mistake when measurement occurred at multiple fourth dimension points, we planned merely to pool data from one meter point that was closest to that of the other included studies.

    Including multiple wounds

    We considered adjusting for clustering when multiple wounds were included in the same patient. We could not find a published standard value for the inter‐cluster correlation ( ICC ) that should be used to adjust for clustering for this scenario. Therefore we explored three likely situations with different values used for ICC, and then performed a sensitivity analysis on the overall effect of the two most extreme scenarios on the overall results.

    Dealing with missing data

    If the results of a trial were published, but information on the consequence of interest was not reported, we attempted, whenever possible, to contact the trial authors for the miss information. If continuous data were not presented as mean and standard deviation, we planned, whenever possible, to contact the trial authors to request the information in this format. If the data were not available, we planned to impute the missing standard deviation by borrowing from similar studies, or we calculated the standard deviation from P values, t values, confidence intervals or standard errors, whichever was available. We followed the methods described in the Cochrane Handbook for Systematic Reviews of Interventions ( Deeks 2011 ). In the completed review, we report all efforts made to obtain extra data. Excluding participants from the analysis after randomization, or ignoring participants lost to follow‐up can, in effect, undo the process of randomization, and thus potentially insert bias into the trial. therefore, where potential, all analyses were to be by intention‐to‐treat ( Hollis 1999 ). If participants were allocated to one interposition ( for exercise, antibiotic cream ), but after randomization underwent a different intervention ( for case, placebo cream ), they were to be analyzed according to their randomization allotment. If the results for dichotomous variables were not reported in some participants, we planned in the first place to base our analysis on both a worst potential result ( for example, wound infection occurred in all not reported cases ), and a best possible consequence ( for model, wound infection did not occur in any not reported cases ). Where participants were excluded from analysis without good lawsuit we planned to conduct a sensitivity analysis to determine any impression of attrition bias.

    Assessment of heterogeneity

    We explored the presence or absence of heterogeneity using ocular inspection of forest plots. If there was no apparent face value heterogeneity ( e.g. intelligibly different populations or types of wounds, different class of control group ) we performed a Chi2 examination with significance set at P measure 0.10. We besides calculated the I2 statistic ( Deeks 2011 ). This explores the proportion of variability caused by heterogeneity rather than by chance. Thresholds for the rendition of the I2 statistic can be misleading. A rough guide to rendition of the I2 statistic is :

    • 0 % to 40 % : might not be important ;
    • 30 % to 60 % : may represent centrist heterogeneity ;
    • 50 % to 90 % : may represent hearty heterogeneity ; and
    • 75 % to 100 % : represents considerable heterogeneity.
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    When interpreting and exploring the I2 statistic, we took factors such as clinical and methodological heterogeneity ‐ in particular the placebo treatment used ‐ along with whether the heterogeneity was in the magnitude of effect or in the direction of effect, into account, peculiarly where ranges overlapped ( Deeks 2011 ). We explored this far in subgroup analyses. We planned that if heterogeneity was very high ( > 75 % ), we would not pool these studies ; we explored the impingement of heterogeneity on the overall result with a sensitivity analysis ( see Sensitivity analysis ).

    Assessment of reporting biases

    We compared the reported outcomes with those stated in the published protocol of the studies, if available, or in the methods section of the published report, and besides those listed in clinical trials registries as both primary and secondary coil outcomes ( for exemplar ). If sufficient studies were identified ( a minimal of 10 ), we planned to assess the risk of issue bias by creating a funnel plot using software within Review Manager 5 ( RevMan 2014 ), using ocular inspection and statistical tests for asymmetry.

    Data synthesis

    One review generator ( CH ) entered quantitative data into Review Manager 5 ( RevMan 2014 ), and a second ( PL ) checked the data. We calculated drumhead estimates of treatment effect ( with 95 % confidence time interval ) for each result and every comparison. For continuous outcomes, we presented the pool think of deviation with the standard deviation as a measure of the dispersed. For dichotomous outcomes, we calculated the hazard proportion as the consequence measure, with 95 % confidence interval. We besides calculated the absolute risk dispute, that would allow us to calculate the NNTB. We meta‐analysed the results of clinically homogeneous studies using Review Manager 5 ( RevMan 2014 ). We conducted meta‐analyses using a random‐effects model. If insufficient data were available for meta‐analyses, we presented a narrative deduction of the consequence across the admit studies. We presented all results in ‘Summary of findings ‘ tables, and rated the quality of evidence using the GRADE system ( see below ) ( Schünemann 2011a ).

    ‘Summary of findings’ tables

    We presented the independent results of the review in ‘Summary of findings ‘ tables. These tables present winder information concerning the timbre of the evidence, the magnitude of the effects of the interventions examined, and the kernel of the available data for the independent outcomes ( Schünemann 2011a ). The ‘Summary of findings ‘ tables besides include an overall marking of the evidence related to each of the main outcomes using the GRADE ( Grades of Recommendation, Assessment, Development and Evaluation ) approach. The GRADE approach defines the quality of a body of attest as the extent to which one can be confident that an estimate of effect or affiliation is close to the truthful quantity of particular interest. The timbre of a body of tell involves consideration of within‐trial risk of diagonal ( methodological choice ), candor of attest, heterogeneity, preciseness of consequence estimates and risk of publication bias ( Schünemann 2011b ). We presented the follow primary outcomes in the `Summary of findings´ tables :

    • superficial surgical locate infection ;
    • adverse events ;
    • the proportion of wounds healed during the time period.

    Subgroup analysis and investigation of heterogeneity

    Where there were sufficient trials of adequate size and it was possible to conduct subgroup analyses, we planned to conduct subgroup analyses for :

    • clean versus clean/contaminated versus contaminated wounds ;
    • dermatologic versus general surgery ;
    • class of antibiotic used ;
    • single application versus multiple applications ; and
    • no treatment operate versus placebo ointment control.

    Sensitivity analysis

    We performed a sensitivity analysis to assess the impact of heterogeneity on the overall estimate of consequence by first pooling all studies, and subsequently removing the outlying studies that seemed to be contributing to the statistical heterogeneity. We besides performed sensitivity analysis to assess the impact of gamble of bias on the overall effect measure. We compared the outcomes of these analyses and described the implications for the conclusion of the revue. We removed studies at high risk of diagonal in club to assess the effect of this on the result.

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