Intracavity lavage and wound irrigation for prevention of surgical site infection.

We included published and unpublished randomised controlled trials (RCTs), including cluster‐RCTs, irrespective of language of report. We excluded studies using quasi‐randomisation (i.e. a method of allocating participants to different forms of care that is not truly random, for example, allocation by date of birth, day of the week, medical record number, month of the year, or the order in which participants are included in the study (alternation)). All patients undergoing elective or emergency surgery, where surgery was defined as a procedure involving: (1) an incision being made into the skin forming an open wound; or (2) an operative procedure to treat an existing traumatic wound/injury. We included studies including either, or both, adults and children. Only studies focusing on wounds intended to heal by primary intention (i.e. where wound edges are held together after surgery) were included in this review. This included interventions for open fractures or operated traumatic wounds if the aim of the procedure was to heal the wound by primary intention. We excluded surgery intended to create wounds with planned healing by secondary intention (i.e. left open to heal through the formation of new tissues) or wounds healing by delayed primary/tertiary intention (wounds which are intentionally initially left open for a period of time, but then have the edges brought together for the rest of the healing process). We included studies where the type or schedule of intraoperative washout (either wound irrigation or intracavity lavage) was the only systematic difference between study arms. Surgical wound irrigation may occur as a singular event during wound closure, or involve the irrigation of a wound continuously/repeatedly during surgery, or in the postoperative period. Types of surgical wound irrigation may vary by volume of irrigation fluid, mechanism of delivery, or solution composition. We did not include studies where the irrigation was confined solely to the interior of internal organs (e.g.) the uterus, bowel or bladder, but did include studies in which (e.g.) the peritoneum was irrigated in addition to such procedures. We did not include studies of surgery in the oral or aural cavities or in the eyes. Intracavity lavage may also occur as a singular event during surgery, which exposes a body cavity, or involve the irrigation of a cavity continuously/repeatedly during surgery, or in the postoperative period. Types of intracavity lavage again may vary by volume of irrigation fluid, mechanism of delivery, or solution composition. In practice we found that the terms 'irrigation' and 'lavage' are often used interchangeably. We included all studies in which a washout procedure was conducted and we have used the term 'irrigation' throughout the review. Where the term 'lavage' was used in the included studies, this is reflected in the Characteristics of included studies tables; this section also details all available information on the point(s) at which irrigation occurred during surgery. We did not pre‐specify any subgrouping based on the use of irrigation or lavage or the level at which it was conducted; we have not conducted any post‐hoc analysis based on this but have followed the protocol and grouped all forms of intraoperative washout. The only exception was where one study used procedures which were so different from the other studies in the comparison that we treated this separately. We anticipated that likely comparisons in this review may include: comparison of wound irrigation/intracavity lavage with no washout; comparison of different solutions used for wound irrigation or intracavity lavage; comparison of different volumes of fluid used for wound irrigation or intracavity lavage; comparison of different mechanisms of delivery used for wound irrigation or intracavity lavage; and comparison of different schedules/timings of wound irrigation or intracavity lavage. comparison of wound irrigation/intracavity lavage with no washout; comparison of different solutions used for wound irrigation or intracavity lavage; comparison of different volumes of fluid used for wound irrigation or intracavity lavage; comparison of different mechanisms of delivery used for wound irrigation or intracavity lavage; and comparison of different schedules/timings of wound irrigation or intracavity lavage. We list primary and secondary outcome measures below. If a trial was otherwise eligible (correct study design, population, and intervention/comparator) but did not report a listed outcome, then we attempted to contact the study authors, in order to establish whether a relevant outcome was measured but not reported. However, we did not plan to exclude otherwise eligible studies solely on the basis of reported outcomes. In several instances author contact was not immediately successful and we recorded these studies as Studies awaiting classification . Where possible, we anticipated grouping outcomes by the following time points; the review authors used their judgement as to whether statistical pooling within these time categories was appropriate: short‐term: 30 days medium‐term: more than 30 days to 12 months long‐term: more than 12 months. short‐term: 30 days medium‐term: more than 30 days to 12 months long‐term: more than 12 months. In practice we found that the overwhelming majority of the data reported were for time points of between two and eight weeks postoperatively, with the majority being at either four or six weeks, sometimes with interim but unreported follow‐up points. We therefore decided that we would group all the data together for the outcomes reported; we did not consider dividing data reported at points that narrowly spanned 30 days to be informative. Surgical site infection measured as: occurrence of postoperative surgical site infection (SSI) as defined by the CDC criteria ( Horan 2008 ), or the study authors' definition of SSI. We did not differentiate between superficial and deep incisional infection. We planned to document septicaemia or septic shock under this outcome. Wound dehiscence within 30 days of operation. This included both superficial dehiscence (involving skin and subcutaneous tissues) or deep dehiscence (burst abdomen or dehiscence of fascia). Postoperative wound dehiscence refers to wound disruption resulting from poor wound healing. This may be caused by various factors, including infection, as well as the type of incision and patient characteristics, such as diabetes or smoking ( Sandy‐Hodgetts 2015 ). Surgical site infection measured as: occurrence of postoperative surgical site infection (SSI) as defined by the CDC criteria ( Horan 2008 ), or the study authors' definition of SSI. We did not differentiate between superficial and deep incisional infection. We planned to document septicaemia or septic shock under this outcome. Wound dehiscence within 30 days of operation. This included both superficial dehiscence (involving skin and subcutaneous tissues) or deep dehiscence (burst abdomen or dehiscence of fascia). Postoperative wound dehiscence refers to wound disruption resulting from poor wound healing. This may be caused by various factors, including infection, as well as the type of incision and patient characteristics, such as diabetes or smoking ( Sandy‐Hodgetts 2015 ). 30‐day mortality/in‐hospital mortality Proportion of participants with postoperative SSI using systemic antibiotics within 30 days of surgery Occurrence of infections that show antibiotic resistance Adverse events including postoperative abscess formation; we planned to include these, where reported, as total number of individuals with an adverse event in each intervention group Surgical re‐intervention rates (including the placement of radiologically‐guided drains and joint revision surgery) Mean length of hospital stay Number of hospital readmissions. 30‐day mortality/in‐hospital mortality Proportion of participants with postoperative SSI using systemic antibiotics within 30 days of surgery Occurrence of infections that show antibiotic resistance Adverse events including postoperative abscess formation; we planned to include these, where reported, as total number of individuals with an adverse event in each intervention group Surgical re‐intervention rates (including the placement of radiologically‐guided drains and joint revision surgery) Mean length of hospital stay Number of hospital readmissions. We searched the following electronic databases for randomised controlled trials: the Cochrane Wounds Specialised Register (searched 1 February 2017); the Cochrane Central Register of Controlled Trials (CENTRAL; 2017, issue 1) in the Cochrane Library (searched 1 February 2017); Ovid MEDLINE (1946 to 1 February 2017); Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations) (searched 1 February 2017); Ovid Embase (1974 to 1 February 2017); EBSCO CINAHL Plus (1937 to 1 February 2017). the Cochrane Wounds Specialised Register (searched 1 February 2017); the Cochrane Central Register of Controlled Trials (CENTRAL; 2017, issue 1) in the Cochrane Library (searched 1 February 2017); Ovid MEDLINE (1946 to 1 February 2017); Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations) (searched 1 February 2017); Ovid Embase (1974 to 1 February 2017); EBSCO CINAHL Plus (1937 to 1 February 2017). The search strategies for the Cochrane Wounds Specialised Register, CENTRAL, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL Plus are available in Appendix 1 . 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) ( Lefebvre 2011 ). We combined the Embase search with the Ovid Embase randomised trials filter terms developed by the UK Cochrane Centre ( Lefebvre 2011 ). We combined the CINAHL Plus searches with the randomised trials filter terms developed by the Scottish Intercollegiate Guidelines Network ( SIGN 2017 ). We did not impose any restrictions with respect to language, date of publication, or study setting. We also searched the following clinical trials registries for ongoing studies in March 2017: ClinicalTrials.gov (searched 7 March 2017); World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (searched 7 March 2017); EU Clinical Trials Register (searched 7 March 2017). ClinicalTrials.gov (searched 7 March 2017); World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (searched 7 March 2017); EU Clinical Trials Register (searched 7 March 2017). Search strategies for the clinical trials registries are available in Appendix 1 . We sought to identify other potentially eligible trials or ancillary publications by searching the reference lists of retrieved included trials as well as relevant systematic reviews, meta‐analyses, and health‐technology assessment reports. Two review authors (CR and either TS or GN) independently assessed the titles and abstracts of the citations retrieved by the searches for relevance. After this initial assessment, we obtained full‐text copies of all studies considered to be potentially relevant. Two review authors (GN and either CR or TS) independently checked the full papers for eligibility; disagreements were resolved by discussion and, where required, the input of a third review author (CR, TS, JD or RA as appropriate). Where required and possible, we contacted study authors where the eligibility of a study was unclear. We recorded all reasons for exclusion of studies for which we had obtained full copies, where it was not immediately obvious that the study was ineligible after being ordered due to a very sparse citation record. We completed a PRISMA flowchart to summarise this process ( Liberati 2009 ); Figure 1 . Study flow diagram Where studies were reported in multiple publications/reports, we obtained all publications. Whilst we included the study only once in the review, we extracted data from all reports to ensure maximal relevant data were obtained. Where it was unclear whether publications referred to the same study we attempted to contact the authors for clarification. We extracted and summarised details of the eligible studies using a data extraction sheet. Two review authors (two of CR,TS, GN, RA and AR) extracted data independently and resolved disagreements by discussion, drawing on a third review author (JD) where required. Where key data were missing from reports, we attempted to contact the study authors to obtain this information. Where a study with more than two intervention arms was included, we only extracted data from intervention and control groups that met the eligibility criteria. We extracted the following data, where possible, by treatment group for the prespecified interventions and outcomes in this review. We planned to collect outcome data for relevant time points, as described in Types of outcome measures ; in practice most studies reported only one time point. Country of origin Type of wound and surgery Unit of randomisation (e.g. participant or wound) Unit of analysis (e.g. participant or wound) Trial design (e.g. parallel; cluster) Number of participants/wounds randomised to each trial arm Eligibility criteria and key baseline participant data Details of treatment regimen received by each group Duration of treatment Details of any co‐interventions Primary and secondary outcome(s) (with definitions and time points) Outcome data for primary and secondary outcomes (by group) Duration of follow‐up. Number of withdrawals (by group) Publication status of study Source of funding for trial. Country of origin Type of wound and surgery Unit of randomisation (e.g. participant or wound) Unit of analysis (e.g. participant or wound) Trial design (e.g. parallel; cluster) Number of participants/wounds randomised to each trial arm Eligibility criteria and key baseline participant data Details of treatment regimen received by each group Duration of treatment Details of any co‐interventions Primary and secondary outcome(s) (with definitions and time points) Outcome data for primary and secondary outcomes (by group) Duration of follow‐up. Number of withdrawals (by group) Publication status of study Source of funding for trial. Two review authors (two of CR, TS, GN, RA or AR) independently assessed included studies using the Cochrane approach for assessing risk of bias as detailed in the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins 2011a ). We resolved disagreements through discussion or by consulting a third review author (typically JD). The tool addresses specific domains: sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessors, incomplete data, selective outcome reporting, and other issues – in this review we planned to record issues with unit of analysis, for example, where a cluster trial had been undertaken but analysed at the individual level in the study report ( Appendix 2 ). We recorded issues with adjustment for paired data in split‐body designs and with early stopping in this domain. We assessed blinding and completeness of outcome data for each of the review outcomes separately. In this review we anticipated that blinding of participants and personnel may not be possible. For this reason the assessment of the risk of detection bias focused on whether blinded outcome assessment was reported (because assessment of wound outcomes, such as breakdown and healing, can be subjective and at high risk of detection bias when outcome assessment is not blinded). We used blinding of outcome assessment to determine risk of bias from blinding in these instances. Although we recorded risk of bias from blinding of personnel and participants, we did not downgrade the certainty of the evidence for this alone, where the nature of the comparison made it highly likely. We presented our assessment of risk of bias using two 'Risk of bias' summary figures; one that is a summary of bias for each item across all studies, and a second that shows a cross‐tabulation of each trial by all of the risk of bias items ( Figure 2 ; Figure 3 ). Risk of bias summary: review authors' judgements about each risk of bias item for each included study Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies For trials using cluster‐randomisation, we also planned to consider the risk of bias considering: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and comparability with individually randomised trials ( Higgins 2011b ; Appendix 3 ). For dichotomous outcomes, we calculated the risk ratio (RR) with 95% confidence intervals (CIs). For continuous outcomes we used the difference in means with 95% CIs, if all trials used the same or similar assessment scale. If trials had used different assessment scales, we planned to use the standardised difference in means with 95% CIs. If included studies had randomised at the participant level and measured outcomes at the wound level, we planned to treat the participant as the unit of analysis when the number of wounds assessed appeared equal to the number of participants (e.g. one wound per person). Particular unit of analysis issues in wound care trials can occur when: (1) studies randomise at the participant level, use the allocated treatment on multiple wounds per participant, and then analyse outcomes per wound; or (2) studies undertake multiple assessments of an outcome over time per participant. These approaches should be treated as cluster trials, alongside more standard cluster designs – such as delivery of interventions at an organisational level. Where a cluster trial had been conducted and correctly analysed we planned to meta‐analyse effect estimates and their standard errors using the generic inverse‐variance method in Review Manager 5 ( RevMan 2014) . We planned to record where a cluster‐randomised trial had been conducted, but incorrectly analysed as part of the 'Risk of bias' assessment. If possible, we planned to approximate the correct analyses based on guidance from the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins 2011b ), using information on: the number of clusters (or groups) randomised to each intervention group; or the average (mean) size of each cluster; the outcome data ignoring the cluster design for the total number of individuals (for example, number or proportion of individuals with events, or means and standard deviations); and an estimate of the intra cluster (or intra class) correlation coefficient (ICC). the number of clusters (or groups) randomised to each intervention group; or the average (mean) size of each cluster; the outcome data ignoring the cluster design for the total number of individuals (for example, number or proportion of individuals with events, or means and standard deviations); and an estimate of the intra cluster (or intra class) correlation coefficient (ICC). If we had been unable to analyse the study data correctly, we planned to extract and present outcome data but not analyse it further. We did not identify any cluster randomised studies, but did identify a split‐body design in which two incisions on each participant were randomised to different treatment groups. This represented paired data and it was unclear that this had been adjusted for. Unadjusted paired data will generate confidence intervals wider than the true ones for the effect estimate. We presented the results of the single study with this design in narrative form, but did not include data from the study in any meta‐analysis. It is common to have data missing from trial reports. Excluding participants post‐randomisation from the analysis, or ignoring those participants who are lost to follow‐up compromises the randomisation, and potentially introduces bias into the trial. Where there were missing data that we thought should be included in the analyses, or where data were unclear, we attempted to contact relevant study authors to request or clarify these data. Where data remained missing for the proportion of participants with dehisced wounds or participants with SSI, we assumed that if randomised participants were not included in the results section of the paper, their wound did not show dehiscence or they did not have a SSI (i.e. in the analysis, missing participants were considered in the denominator but not the numerator). When appropriate, we planned to conduct a completed case analysis as a sensitivity analysis and also planned to explore alternative scenarios using different assumptions about missing cases. In the event only one trial had very substantive numbers of participants who were absent from the reported results and, because of clinical considerations we considered an ITT analysis non‐conservative. We therefore conducted a completed case analysis and conducted a sensitivity analysis to explore the impact of excluding this trial from the meta‐analysis. For continuous variables, for example, length of hospital stay, and for all secondary outcomes, we presented available data from the study reports/study authors, but we did not impute missing data. Where measures of variance were missing, we planned to calculate these if this were possible. When calculation was not possible, we attempted to contact study authors. Where these measures of variation were not available, we excluded the study from any relevant meta‐analyses that we conducted. Assessment of heterogeneity can be a complex, multifaceted process. Firstly, we considered clinical and methodological heterogeneity: that is, the degree to which the included studies varied in terms of participant, intervention, outcome, and characteristics such as duration of follow‐up. We supplemented this assessment of clinical and methodological heterogeneity with information regarding statistical heterogeneity ‐ assessed using the Chi² test (we considered a significance level of P < 0.10 to indicate statistically significant heterogeneity) in conjunction with the I² statistic ( Higgins 2003 ). The I² statistic examines the percentage of total variation across RCTs that is due to heterogeneity rather than chance ( Higgins 2003 ). In general, I² values of 25%, or less, can be interpreted as a low level of heterogeneity ( Higgins 2003 ), and values of 75%, or more, indicate very high heterogeneity ( Deeks 2011 ). However, these figures are only a guide, and it has been recognised that statistical tests and metrics may miss important heterogeneity ‐ thus, whilst these were assessed, the overall assessment of heterogeneity used these measures in combination with the methodological and clinical assessment of heterogeneity: see Data synthesis for further information about how we dealt with potential heterogeneity in the data analyses. Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. Publication bias is one of a number of possible causes of 'small study effects', that is, a tendency for estimates of the intervention effect to be more beneficial in smaller RCTs. Funnel plots allow a visual assessment of whether small study effects may be present in a meta‐analysis. A funnel plot is a simple scatter plot of the intervention effect estimates from individual RCTs against some measure of each trial's size or precision ( Sterne 2011 ). We presented funnel plots for meta‐analyses comprising 10 RCTs or more using Review Manager 5 ( RevMan 2014 ). We also conducted Egger's test as a post‐hoc measure on the advice of peer reviewers. We combined details of included studies in narrative review according to type of comparator and contamination level of wound. We planned to group outcomes by time period but in practice found that this was not helpful (see Differences between protocol and review ). We considered clinical and methodological heterogeneity, and undertook pooling when studies appeared appropriately similar in terms of wound type, intervention type, duration of follow‐up, and outcome type. In terms of meta‐analytical approach, our default approach was to use the random‐effects model. We planned to only use a fixed‐effect approach if clinical heterogeneity was thought to be minimal and statistical heterogeneity was not statistically significant for the Chi‐ 2 value and 0% for the I 2 assessment ( Kontopantelis 2013 ). We adopted this approach as it is recognised that statistical assessments can miss potentially important between‐study heterogeneity in small samples, hence the preference for the more conservative random‐effects model ( Kontopantelis 2012 ). Since either clinical or statistical heterogeneity indicated that a random‐effects analysis was appropriate in all cases, we did not use any fixed‐effect analyses. Where clinical heterogeneity was thought to be acceptable, or of interest, we planned that we would meta‐analyse even when statistical heterogeneity was high, but would have attempted to interpret the causes behind this heterogeneity. We planned to consider using meta‐regression for that purpose, if possible ( Thompson 1999 ). In the event, heterogeneity was not sufficiently high to require this approach but we used some exploratory subgroup analyses to confirm that lower levels of heterogeneity were not a consequence of particular differences between interventions. We presented data using forest plots, where possible. For dichotomous outcomes, we presented the summary estimate as a RR with 95% CI. If continuous outcomes were measured in the same way across studies, we presented a pooled difference in means with 95% CI; we had planned to pool standardised difference in means estimates where studies measured the same outcome, but use different methods. However the studies that reported continuous data all used the same unit of measurement. For time to event data, we planned to plot (and, if appropriate, pool) estimates of hazard ratios and 95% CIs, as presented in the study reports, using the generic inverse variance method in Review Manager 5 ( RevMan 2014 ), however no time‐to event data were reported in included studies. We obtained pooled estimates of treatment effect using Cochrane Review Manager 5 software ( RevMan 2014 ). We presented the main results of the review in 'Summary of findings' tables. These tables present key information concerning the quality of the evidence, the magnitude 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 also include an overall grading 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 evidence as the extent to which one can be confident that an estimate of effect or association is close to the true quantity of specific interest. The 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 ). GRADE was undertaken for all outcomes where it was possible to calculate an estimate of effect. We planned to present the following primary outcomes in the 'Summary of findings' tables: surgical site infection (SSI); wound dehiscence within 30 days of operation. surgical site infection (SSI); wound dehiscence within 30 days of operation. In addition we also included adverse events in the 'Summary of findings' tables; this was at the suggestion of peer reviewers as noted in Differences between protocol and review . We did not produce a 'Summary of findings' table for comparisons where the data were limited. Instead we summarised the specified outcomes together with their GRADE assessment in an additional table, Table 4 . This was done in order to make the 'Summary of findings' tables manageable and improve the readability of the review. 1 Three‐armed trial; not all participants relevant to this comparison.
 2 Five‐armed trial; not all participants relevant to this comparison. CI: confidence interval; RCT: randomised controlled trial; RR: risk ratio; SSI: surgical site infection Where feasible, we planned to explore the effects of interventions in children (aged under 18) and adults separately. We also planned in advance, and conducted (where possible) an exploration of the effects of interventions according to classification of wound contamination (clean, clean‐contaminated, contaminated, dirty). We used a post‐hoc exploratory sub‐group analysis to confirm the appropriateness of combining studies that used different types of lavage solution. Where possible, we planned and conducted sensitivity analyses to explore the effect of the following criteria: studies at high risk of bias for any domain compared with other studies with no domain classed at high risk of bias; studies at high risk of detection bias compared with other studies. studies at high risk of bias for any domain compared with other studies with no domain classed at high risk of bias; studies at high risk of detection bias compared with other studies. Elements of this Methods section are based on the standard Cochrane Wounds Protocol Template. The published protocol is archived in the Cochrane Library ( Smith 2016 ).

The electronic searches identified 605 records. Of these we obtained 182 full‐text records. Citation searching identified a further 29 records, which were thoroughly assessed as full texts. An additional six records of relevant ongoing studies were identified from searches of trials registers. The results of the search and assessment process are shown in Figure 1 . We included 59 RCTs reported in 64 publications and together involving 14,738 participants. Most included studies assessed the following comparisons. Use of irrigation compared with no irrigation (20 studies) ( Bourgeois 1985 ; Buanes 1991 ; Cervantes‐Sanchez 2000 ; Cho 2004 ; De Jong 1982 ; Elliott 1986 ; Gungorduk 2010 ; Harrigill 2003 ; Mahomed 2016 ; Oleson 1980 ; Ozlem 2015 ; Platt 2003 ; Schein 1990 ; Snow 2016 ; St Peter 2012 ; Tanaka 2015 ; Tanphiphat 1978 ; Temizkan 2016 ; Tighe 1982 ; Viney 2012 ) Use of an antibacterial (antibiotic or antiseptic) solution compared with a non‐antibacterial irrigant such as saline (36 studies) ( Al‐Shehri 1994 ; Baker 1994 ; Bourgeois 1985 ; Browne 1978 ; Carl 2000 ; Case 1987 ; Chang 2006 ; Cheng 2005 ; Dashow 1986 ; Greig 1987 ; Halsall 1981 ; Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ; Levin 1983 ; Lord 1983 ; Magann 1993 ; Marti 1979 ; Mirsharifi 2008 ; Moylan 1968 ; Neeff 2016 ; Oleson 1980 ; Oller 2015 ; Oestreicher 1989 ; Rambo 1972 ; Ruiz‐Tovar 2011 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Ruiz‐Tovar 2016b ; Schein 1990 ; Silverman 1986 ; Sindelar 1979 ; Takesue 2011 ; Tighe 1982 ; Vallance 1985 ) Different methods of irrigation delivery (standard or pulsatile) compared (two studies) ( Hargrove 2006 ; Nikfarjam 2014 ) Different antibacterial irrigants compared (six studies) ( Dashow 1986 ; Mohd 2010 ; Oller 2015 ; Peterson 1990 ; Tighe 1982 ; Vallance 1985 ) Different non‐antibacterial irrigants compared (three studies) ( Brown 2007 ; Shimizu 2011 ; Trew 2011 ) Use of irrigation compared with no irrigation (20 studies) ( Bourgeois 1985 ; Buanes 1991 ; Cervantes‐Sanchez 2000 ; Cho 2004 ; De Jong 1982 ; Elliott 1986 ; Gungorduk 2010 ; Harrigill 2003 ; Mahomed 2016 ; Oleson 1980 ; Ozlem 2015 ; Platt 2003 ; Schein 1990 ; Snow 2016 ; St Peter 2012 ; Tanaka 2015 ; Tanphiphat 1978 ; Temizkan 2016 ; Tighe 1982 ; Viney 2012 ) Use of an antibacterial (antibiotic or antiseptic) solution compared with a non‐antibacterial irrigant such as saline (36 studies) ( Al‐Shehri 1994 ; Baker 1994 ; Bourgeois 1985 ; Browne 1978 ; Carl 2000 ; Case 1987 ; Chang 2006 ; Cheng 2005 ; Dashow 1986 ; Greig 1987 ; Halsall 1981 ; Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ; Levin 1983 ; Lord 1983 ; Magann 1993 ; Marti 1979 ; Mirsharifi 2008 ; Moylan 1968 ; Neeff 2016 ; Oleson 1980 ; Oller 2015 ; Oestreicher 1989 ; Rambo 1972 ; Ruiz‐Tovar 2011 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Ruiz‐Tovar 2016b ; Schein 1990 ; Silverman 1986 ; Sindelar 1979 ; Takesue 2011 ; Tighe 1982 ; Vallance 1985 ) Different methods of irrigation delivery (standard or pulsatile) compared (two studies) ( Hargrove 2006 ; Nikfarjam 2014 ) Different antibacterial irrigants compared (six studies) ( Dashow 1986 ; Mohd 2010 ; Oller 2015 ; Peterson 1990 ; Tighe 1982 ; Vallance 1985 ) Different non‐antibacterial irrigants compared (three studies) ( Brown 2007 ; Shimizu 2011 ; Trew 2011 ) No studies compared an antibiotic solution with an antiseptic and no studies compared different volumes of irrigation. There were eleven studies with more than two relevant arms ( Bourgeois 1985 ; Dashow 1986 ; Elliott 1986 ; Levin 1983 ; Magann 1993 ; Marti 1979 ; Oleson 1980 ; Oller 2015 ; Tighe 1982 ; Schein 1990 ; Vallance 1985 ); where appropriate to the comparison we combined data from two or more arms. A majority of included studies enrolled adult participants. A small number ( Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ; St Peter 2012 ) included only children, and in several others there were a mixture of adult and paediatric participants or it was unclear whether children, adults or a mixture were included. More information on study participants is given for each comparison (see Effects of interventions ). Because of the nature of the surgeries assessed (e.g. caesarean sections), many studies enrolled only women. A wide range of surgical operations and all classes of surgery (clean, clean‐contaminated, contaminated, dirty) were represented in the review. Use of prophylactic antibiotics varied but was, as anticipated, more likely to be reported for studies enrolling participants undergoing surgeries with higher levels of contamination. For further details of the operations and surgical category represented in each comparison (see Effects of interventions ). Five studies (reported in six publications) are pending assessment ( De Cicco 2015 ; De Kok 1998 ; Kosuş 2010 ; Munoz‐Mahamud 2011 ; Taylor 1999 ). In each case there were no relevant review outcomes reported; we have attempted to contact study authors without success to date in four cases. In the case of De Cicco 2015 a further publication with relevant data is pending but the corresponding author was unable to supply this in advance of publication. We were able to exclude a further study after author contact confirmed that the purpose of the study was outside the scope of this review and no relevant outcome data were available ( Keblawi 2006 ) (see Excluded studies ). Searching of trial registers identified six additional studies, which appeared to meet inclusion criteria but which were either still ongoing or which were completed but had no available outcome data or related publications. See Ongoing studies for details of these trials. We excluded 141 papers after appraisal of the full text. We ordered many of these because the initial records contained so little information, and upon obtaining full texts it was immediately evident that many studies were not eligible; others were reviews obtained solely in order to screen the bibliography. We noted more nuanced reasons for exclusion for 73 studies reported in 78 records; these studies are detailed here (see Characteristics of excluded studies ). We excluded studies for the following reasons: use of quasi‐randomisation (14 studies: Al‐Ramahi 2006 ; Bertheussen 1980 ; Bhargava 2006 ; Geraghty 1984 ; Iqbal 1998 ; Kellum 1985 ; Ko 1992 ; Makvandi 2014 ; Nachamie 1968 ; Nomikos 1986 ; Noon 1967 ; Rogers 1983 ; Salvati 1988 ; Sood 1985 ); or lack of randomisation only apparent after translation or study author contact (two studies: Terzi 2015 ; Wu 1992 ); use of perioperative irrigation was not the only systematic difference between groups (20 studies: Alcantara 2011 ; Badia 1994 ; Bennett‐Guerrero 2016 ; Boothby 1984 ; Donnenfeld 1986 ; Ducharme 1986 ; Fountas 1999 ; Freischlag 1984 ; Garg 2013 ; Gonen 1986 ; Kothuis 1981 ; Mathelier 1992 ; Pollock 1978 ; Sarr 1988 ; Sauven 1986 ; Scheuerlein 2000 ; Shapiro 1986 ; Toki 1995 ; White 2008 ; Xiao 2010 ); the study enrolled participants from a different patient population ‐ some or all participants did not undergo surgery (eight studies: Chisholm 1992 ; Ghafouri 2016a ; Ghafouri 2016b ; Granick 2007 ; Longmire 1987 ; Morse 1998 ; Rosen 1985 ; Weiss 2013 ) or there was healing by delayed primary or secondary intention in some or all wounds (12 studies: Akay 2006 ; Anglen 2005 ; Angobaldo 2008 ; FLOW 2011 ; Galle 1980 ; Hesami 2014 ; Hunt 1982 ; Martins 2012 ; Plaumann 1985 ; Scammell 1985 ; Sherman 1976 ; Sindelar 1985 ); the study assessed an ineligible intervention including irrigation conducted as a method of analgesia only, volumes of liquid used being too low to be considered irrigation, or irrigation was not the intervention of interest (17 studies: Cherian 2000 ; Dwivedi 2009 ; Everett 1969 ; Georgiadis 2013 ; Givens 2002 ; Horn 1999 ; Iqbal 2015 ; Keblawi 2006 ; Lau 1986 ; Lavery 1986 ; Logan 1973 ; Mohamed 2017 ; Pitt 1982 ; Pobereskin 2000 ; Sarzaeem 2014 ; Seco 1990 ; Yarussi 1999 ). A minority of studies were at high risk of avoidable bias in one or more domains. Many more were at risk of performance bias because of the nature of the comparison evaluated, and in more still there was a lack of clarity about the risk of bias across many or even all domains. The risk of bias for each study and a summary across all studies is shown in Figure 2 and Figure 3 . About half of the included studies reported appropriate methods of generating a randomisation sequence. The others had an unclear risk of bias with the exception of one where it appeared that an otherwise acceptable method was likely not to have been implemented and the authors noted concern that randomisation may have been compromised ( Tanphiphat 1978 ). Fewer studies reported adequate concealment of allocation; in a majority this was unclear. Many of the studies assessed a comparison between lavage/irrigation and no lavage/irrigation. In these cases personnel could not be blinded and the studies were therefore at high risk of performance bias. Because of this we focused on blinding of outcome assessment (risk of detection bias) when performing the GRADE assessment for these comparisons and did not downgrade because of high risk of performance bias. Where blinding was more feasible it often remained unclear whether personnel and participants were aware of the treatment groups. Blinding of outcome assessors was reported for a minority of studies. While only a few studies were clearly at high risk of detection bias many more had an unclear risk as the assessment was poorly described. Almost two‐thirds of studies were classed as being at low risk of bias for this domain. However a minority of studies were at high risk of bias with exclusions from analyses representing a serious threat to the validity of the result. A minority of studies showed clear evidence of reporting bias. A somewhat greater number clearly reported full details of all specified outcomes, but many more were poorly reported and it was unclear whether all planned outcomes were fully reported. There were few additional sources of bias which were evident from the trial reports but many studies were poorly or very briefly reported and it was difficult to determine whether there were additional factors that we may have considered to pose a serious risk of bias. See: Table 1 ; Table 2 ; Table 3 We assessed the following types of comparisons. Comparison of irrigation with no irrigation Comparisons of different types of irrigation solution antibacterial (antibiotic or antiseptic) versus non‐antibacterial comparisons of different antibacterial solutions ‐ either two antibiotics or two antiseptics comparisons of different non‐antibacterial solutions Comparisons of different methods of lavage delivery. Comparison of irrigation with no irrigation Comparisons of different types of irrigation solution antibacterial (antibiotic or antiseptic) versus non‐antibacterial comparisons of different antibacterial solutions ‐ either two antibiotics or two antiseptics comparisons of different non‐antibacterial solutions Comparisons of different methods of lavage delivery. Table 1 Twenty studies (7192 participants) compared the use of some form of wound irrigation with no irrigation. Types of surgery represented in this comparison include breast surgery (reduction), caesarean sections, appendicitis surgery, gastrectomy, uterine surgery, liver resection and various abdominal procedures and cover clean, clean‐contaminated, contaminated and dirty surgical classifications. One study was classed as clean ( Platt 2003 ); nine as clean‐contaminated ( Bourgeois 1985 ; Cho 2004; Elliott 1986 ; Gungorduk 2010 ; Harrigill 2003 ; Mahomed 2016 ; Tanaka 2015 ; Temizkan 2016 ; Viney 2012 ); three as contaminated ( Cervantes‐Sanchez 2000 ; Tanphiphat 1978 ; Tighe 1982 ) and five as dirty ( Buanes 1991 ; Oleson 1980 ; Ozlem 2015 , Schein 1990 ; St Peter 2012 ). Two studies included surgical procedures in several categories ( De Jong 1982 ; Snow 2016 ). One of the studies enrolled only children ( St Peter 2012 ); 11 enrolled only adults ( Bourgeois 1985 ; Elliott 1986 ; Gungorduk 2010 ; Harrigill 2003 ; Mahomed 2016 ; Platt 2003 ; Schein 1990 ; Snow 2016 ; Tanaka 2015 ; Temizkan 2016 ; Viney 2012 ) and in eight studies the population was mixed or unclear ( Buanes 1991 ; Cervantes‐Sanchez 2000 ; Cho 2004; De Jong 1982 ; Oleson 1980 ; Ozlem 2015 ; Tanphiphat 1978 ; Tighe 1982 ). The type of solution used for irrigation varied and included saline (15 studies, 2667 participants Bourgeois 1985 ; Buanes 1991 ; Cervantes‐Sanchez 2000 ; Cho 2004; Gungorduk 2010 ; Harrigill 2003 ; Oleson 1980 ; Ozlem 2015 , Platt 2003 ; Schein 1990 ; Snow 2016 ; St Peter 2012 ; Tanaka 2015 ; Temizkan 2016 ; Viney 2012 ), an alternative without antibacterial properties (1 study, 131 participants Tighe 1982 ), different antiseptic solutions (4 studies, 4367 participants De Jong 1982 ; Mahomed 2016 ; Tanphiphat 1978 ; Tighe 1982 ), and solutions containing various antibiotics or combinations of antibiotics (4 studies, 501 participants Bourgeois 1985 ; Elliott 1986 ; Oleson 1980 ; Schein 1990 ). Antiseptics used included povidone iodine, chlorhexidine and cetrimide (Savlon) and super‐oxidised water (Dermacyn); antibiotics used were cefoxitin, cefamandole, ampicillin or chloramphenicol. Doses and concentrations of both antibiotics and antiseptics varied; full details are given in Characteristics of included studies . Three three‐arm studies randomised participants to no treatment, antibiotic irrigation or saline irrigation ( Bourgeois 1985 ; Oleson 1980 ; Schein 1990 ); another randomised participants to no treatment, antiseptic irrigation or sterile water irrigation ( Tighe 1982 ). In each case we combined the antibiotic or antiseptic and non‐antibacterial interventions and compared them with 'no irrigation'. One four‐arm study ( Elliott 1986 ) used a factorial design to assess antibiotic irrigation and intravenous antibiotics; we combined the arms that used antibiotic irrigation and compared them with the combined arms that used no irrigation. One study Buanes 1991 compared additional postoperative irrigation with no additional treatment following intraoperative irrigation in both arms. We considered this intervention to be substantively different from the comparisons assessed in the other studies and did not include it in the meta‐analyses conducted. One study ( Platt 2003 ) used a 'split‐body' or intra‐individual design, where the two operative sites on each participant were randomised to the two intervention groups. We also excluded this study from the meta‐analysis because it was unclear whether the analysis adjusted for the use of paired data. Fifteen studies with 6297 participants reported analysable data for the outcome of SSI, which was variously defined (some studies did not provide a definition) ( Cervantes‐Sanchez 2000 ; Cho 2004 ; De Jong 1982 ; Elliott 1986 ; Gungorduk 2010 ; Harrigill 2003 ; Mahomed 2016 ; Oleson 1980 ; Ozlem 2015 ; Platt 2003 ; Schein 1990 ; Snow 2016 ; Tanaka 2015 ; Tanphiphat 1978 ; Temizkan 2016 ). Tighe 1982 did not report the number of events in each group and Platt 2003 was not included in the analysis because of the split‐body design employed. Details for all studies are given in Table 5 . 1 Elliott is a 4‐armed trial with a factorial design, arms with and without intravenous antibiotics are combined CI: confidence interval; CSF: cerebrospinal fluid; NR: not reported; RR: risk ratio There is, on average, no clear difference in the incidence of SSI between groups treated with irrigation of any type and those not treated with irrigation. The overall RR was 0.87 (95% CI 0.68 to 1.11; I 2 = 28%) Analysis 1.1 . This was based on 14 trials with 6106 participants. This was low‐certainty evidence downgraded once for risk of bias across various domains in studies that contributed almost half the weight of the analysis, and once for imprecision because confidence intervals included both no effect and values suggesting both harm and benefit. In absolute terms this equates to 13 fewer SSIs per 1000 with irrigation than with no irrigation, with 95% CI from 31 fewer to 10 more SSIs. We assessed whether the analysis may be affected by publication bias; it was not clear that this was the case although we considered it to be possible, but did not downgrade for this ( Figure 4 ). Funnel plot of comparison 1: all irrigation versus no irrigation, outcome: 1.1 surgical site infection We conducted planned subgroup analysis based on the category of surgery, grouping the studies with a mixture of surgery categories ( De Jong 1982 ; Snow 2016 ) with the most high‐risk category represented; in this case, this was dirty surgery. There was only one study of participants undergoing clean surgery, Platt 2003 , which was excluded from the analysis due to the 'split‐body' design used. There were also only three studies of participants undergoing dirty surgery, one of which was extremely small ( Ozlem 2015 ; 14 participants). Because of this, we decided to group clean and clean‐contaminated studies together, and similarly to group contaminated, dirty and mixed studies together. The RR for SSI for the clean‐contaminated sub‐group was 1.00 (95% CI 0.82 to 1.21). The RR for SSI for contaminated or dirty surgeries was 0.74 (95% CI 0.47 to 1.16). Category of surgery may explain some differences between estimates of effect in the included studies; the I 2 for subgroup differences was 29.1%. We could not carry out planned subgroup analysis for this comparison, based on whether participants were adults or children, as only one study ( St Peter 2012 ) enrolled only children, and it did not report SSI data. We undertook an exploratory post‐hoc subgroup analysis of the type of irrigation solution (non‐antibacterial, antiseptic, antibiotic) to test the rationale for combining all studies comparing irrigation with no irrigation in the same comparison. This analysis did not explain the heterogeneity (I 2 for subgroup differences = 0%), supporting the analysis plan employed. The results of this exploratory analysis are shown in Table 6 . CI: confidence interval; RR: risk ratio We conducted a planned sensitivity analysis excluding studies at high risk of bias. All studies were at high risk of bias for blinding of personnel so we excluded studies at high risk of bias in additional domains. Excluding five studies gave an overall effect estimate of RR 0.94 (95% CI 0.77 to 1.16), which is not materially different to the main analysis. Results for the two subgroups were, respectively, clean‐contaminated: RR 0.95 (95% CI 0.77 to 1.19) and contaminated/dirty/mixed: RR 0.82 (95% CI 0.42 to 1.61). We conducted another planned sensitivity analysis excluding studies at high risk of detection bias; this excluded only one study in the clean‐contaminated group and also did not materially change the estimate of effect RR 0.79 (95% CI 0.61 to 1.04); the RR for the clean‐contaminated group was 0.95 (95% CI 0.76 to 1.17). We had decided to exclude Platt 2003 from the analysis because of the split‐body design; however the study reported no events in either arm so no estimate of effect could be calculated and no weight would have been contributed to the analysis. In one study ( De Jong 1982 ), there was more than one wound per person in some cases and wounds rather than participants were the unit of analysis. There were also a substantial number of post‐randomisation exclusions due to death or need for reoperation. Because we were uncertain about the number of wounds in the excluded participants, and because the reasons for exclusion made an assumption that these participants did not have an SSI doubtful, we have reported the completed case analysis for this study and examined the impact of excluding it from the meta‐analysis in a post‐hoc sensitivity analysis. Excluding De Jong 1982 made little difference to the estimate of effect, either overall (RR 0.84, 95% CI 0.62 to 1.14) or in the subgroup of contaminated, dirty or mixed surgeries (RR 0.69, 95% CI 0.38 to 1.25). Buanes 1991 compared additional postoperative irrigation with no additional treatment following intraoperative irrigation in both arms in 83 participants with generalised peritonitis; we analysed this trial separately as a substantively different clinical comparison and showed an increased rate of SSI in the group given additional postoperative irrigation: RR of 5.08 (95% CI 1.17 to 22.09). This was low‐certainty evidence, which was downgraded twice for imprecision due to small numbers of participants and very wide confidence intervals. Only Platt 2003 reported data on wound dehiscence. This split‐body design study conducted in 30 women undergoing clean breast surgery did not clearly adjust for the use of paired data; unadjusted paired data may produce wider confidence intervals than should be the case. There may be little or no difference in the incidence of wound dehiscence (RR 1.17, 95% CI 0.44 to 3.06). This was low‐certainty evidence downgraded twice for imprecision due to small numbers, wide confidence intervals and uncertainty about the analysis. Three studies reported analysable data on overall adverse events ( Harrigill 2003 ; Ozlem 2015 ; Tanaka 2015 ). Three other studies focused specifically on abscess formation, which we had prespecified as a specific event of interest ( Oleson 1980 ; Snow 2016 ; St Peter 2012 ); Ozlem 2015 reported one abscess but did not state in which group it occurred. Other studies reported only specific additional complications ( Bourgeois 1985 ; Elliott 1986 ) or information that was not group‐specific ( Cervantes‐Sanchez 2000 ). Current trial evidence shows that, on average, there is no clear difference in the total number of adverse events between groups treated with irrigation and those treated with no irrigation (RR 1.05, 95% CI 0.76 to 1.44, I 2 = 0%; 403 participants) (low‐certainty evidence downgraded once for imprecision and once for high risk of detection bias in the study with 78% of the analysis weight) Analysis 1.2 . There is also no clear difference in the number of participants with abscess formation (RR 0.91, 95% CI 0.54 to 1.54, I 2 = 0%, 331 participants) (moderate‐certainty evidence downgraded once for imprecision) Analysis 1.3 . Two studies reported data on mortality explicitly ( Schein 1990 ; Tanaka 2015 ). On average, there is no clear difference in mortality between the irrigation and no irrigation groups in these studies; the confidence intervals are wide and likely to be fragile, they also span both benefit and harm (RR 0.86, 95% CI 0.36 to 2.04, I 2 = 0%, 280 participants). This was low‐certainty evidence downgraded twice for imprecision Analysis 1.4 . Nine studies with 1949 participants reported some data on hospital stay. Seven (1597 participants) reported data on mean length of stay ( Bourgeois 1985 ; Elliott 1986 ; Gungorduk 2010 ; Harrigill 2003 ; Schein 1990 ; St Peter 2012 ; Tanaka 2015 ) and three (352 participants) reported median length of stay ( Oleson 1980 ; Snow 2016 ; Viney 2012 ). There is, on average, little or no difference in the length of stay between the irrigation and no irrigation groups; the difference in means was ‐0.13 days (95% CI ‐0.38 to 0.12; I 2 = 82%) Analysis 1.5 . This was moderate‐certainty evidence, downgraded once for risk of bias in one or more domains (other than performance bias) in studies accounting for more than 50% of the analysis weight. The studies reporting medians did not demonstrate differences between the groups either ( Table 7 ). More details of interventions can be found in Table 4 and Characteristics of included studies 1 Elliott is a four‐armed trial with a factorial design, arms with and without iv antibiotics are combined CI: confidence interval; CSF: cerebrospinal fluid; MRI: magnetic resonance imaging; MRSA: methicillin‐resistant Staphylococcus aureus ; RR: risk ratio; SSI: surgical site infection The study that we considered too clinically dissimilar to be included in meta‐analysis ( Buanes 1991 ) reported median length of stay as 5 days in both groups with ranges of 3 to 11 days with postoperative irrigation compared with 4 to 12 days without. One large study, Mahomed 2016 , reported the proportion of participants returned to theatre after irrigation with povidone iodine compared with no irrigation in women undergoing caesarean sections; a smaller study reported this in children with appendicitis and used saline irrigation compared with no irrigation ( St Peter 2012 ). There were a total of 3490 randomised participants but a completed case analysis was reported for Mahomed 2016 so 3247 were analysed. Event rates were low and evidence from these studies was that, on average, there is no clear difference between the groups (RR 0.72, 95% CI 0.28 to 1.84; I 2 = 0%) Analysis 1.6 . This was low‐certainty evidence downgraded twice for imprecision due to the very low event rates that led to wide confidence intervals, which included both no effect and values suggesting both harm and benefit. Mahomed 2016 and St Peter 2012 (total of 3490 randomised participants with 3247 included in the completed case analysis) reported the proportion of participants re‐admitted to hospital. From these studies it is uncertain whether there is a difference between the groups on this measure: RR 0.70 (95% CI 0.10 to 4.90 ; I 2 = 53%) Analysis 1.7 . This was very low certainty evidence downgraded twice for imprecision due to the low event rates, which led to wide confidence intervals (despite including 3247 participants) and because the 95% CIs span both benefit and harm as well as no effect, and once for inconsistency between the study estimates. Only Tighe 1982 reported this outcome and the data were not reported by treatment group so no estimate of effect was possible and no full GRADE assessment could be performed ( Table 7 ); the certainty of this evidence is affected by risk of bias as well as imprecision. No studies reported the occurrence of wound infections with antibiotic resistance. Twenty studies assessed a comparison of irrigation and no intervention; 15 of these, with over 6000 participants, reported SSI outcome data. Based on the included trial evidence there is currently no clear difference in incidence of SSI between participant groups treated with irrigation and those given no irrigation. Planned subgroup analysis found that this was the case in each of the surgical contamination subgroups we were able to assess (clean‐contaminated versus contaminated or dirty). Exploratory analysis supported our clinical opinion that it was reasonable to group irrigation solutions with different antibacterial properties together. This was low‐certainty evidence, which was downgraded once due to relevant risks of bias and once due to imprecision. There were no studies included in the analysis that had been conducted in clean surgeries therefore the results may be only indirectly relevant to these operations. A single, small, split‐body design study in clean surgery was the only study to report wound dehiscence: this single study provides low‐certainty evidence reporting no clear difference between groups; downgrading was due to very serious imprecision. Table 2 Thirty‐six studies (6163 participants) compared the use of an antibacterial irrigation with non‐antibacterial irrigation solution. The specific surgery types represented included appendicitis surgery, including perforated appendices; breast surgery (mastectomy or other); cardiac (pacemaker pocket) surgery; gastrointestinal and colorectal surgeries; caesarean sections; surgery for peritonitis; spinal surgery; orthopaedic (hip, pelvic and femoral) surgery; various abdominal procedures; uterine surgery; and general (mixed) surgical populations. All categories of surgery (clean, clean‐contaminated, contaminated, dirty) were represented. We classed eight studies as clean ( Case 1987 ; Chang 2006 ; Cheng 2005 ; Dashow 1986 ; Kokavec 2008 ; Magann 1993 ; Oller 2015 ; Ruiz‐Tovar 2013 ); 12 as clean‐contaminated ( Bourgeois 1985 ; Baker 1994 ; Carl 2000 ; Levin 1983 ; Mirsharifi 2008 ; Moylan 1968 ; Neeff 2016 ; Ruiz‐Tovar 2011 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2016a ; Ruiz‐Tovar 2016b ; Takesue 2011 ); three as contaminated ( Al‐Shehri 1994 ; Marti 1979 ; Tighe 1982 ) and six as dirty ( Browne 1978 ; Kubota 1999 ; Kubota 2015 ; Oleson 1980 ; Rambo 1972 ; Schein 1990 ). Seven studies included surgeries in several categories ( Greig 1987 ; Halsall 1981 ; Lord 1983 ; Oestreicher 1989 ; Silverman 1986 ; Sindelar 1979 ; Vallance 1985 ). We grouped these with the most contaminated class represented in each study (dirty in each case). Three of the studies enrolled only children ( Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ); 19 enrolled only adults Baker 1994 ; Bourgeois 1985 ; Carl 2000 ; Case 1987 ; Dashow 1986 ; Chang 2006 ; Cheng 2005 ; Levin 1983 ; Lord 1983 ; Magann 1993 ; Mirsharifi 2008 ; Oller 2015 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Ruiz‐Tovar 2016b ; Schein 1990 ; Silverman 1986 ; Takesue 2011 ) and in 13 studies the population was mixed or unclear ( Al‐Shehri 1994 ; Browne 1978 ; Greig 1987 ; Marti 1979 ; Moylan 1968 ; Neeff 2016 ; Oestreicher 1989 ; Oleson 1980 ; Rambo 1972 ; Ruiz‐Tovar 2011 ; Sindelar 1979 ; Tighe 1982 ; Vallance 1985 ). In all except two studies the non‐antibacterial irrigant was saline; one study used sterile water ( Tighe 1982 ) and one used Ringer's solution ( Neeff 2016 ). Fourteen studies (3261 participants) used an antiseptic solution ( Baker 1994 ; Browne 1978 ; Chang 2006 ; Cheng 2005 ; Halsall 1981 ; Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ; Neeff 2016 ; Oestreicher 1989 ; Sindelar 1979 ; Takesue 2011 ; Tighe 1982 ; Vallance 1985 ). Vallance 1985 was a three‐armed study that randomised participants to saline or one of two different antiseptic solutions; for this comparison we combined the two antiseptic groups and compared them with saline; the comparison between the two antiseptics is assessed in comparison 5. Antiseptic agents used included povidone iodine (Betadine), chlorhexidine, polyhexanide, taurolidine (Taurolin), and acidic electrolysed water. Twenty‐two studies (2902 participants) used an antibiotic solution ( Al‐Shehri 1994 ; Bourgeois 1985 ; Carl 2000 ; Case 1987 ; Dashow 1986 ; Greig 1987 ; Levin 1983 ; Lord 1983 ; Magann 1993 ; Marti 1979 ; Mirsharifi 2008 ; Moylan 1968 ; Oleson 1980 ; Oller 2015 ; Rambo 1972 ; Ruiz‐Tovar 2011 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Ruiz‐Tovar 2016b ; Schein 1990 ; Silverman 1986 ). Levin 1983 ; Marti 1979 and Oller 2015 were all three‐arm trials assessing saline and two different antibiotic solutions; for this comparison we combined the two antibiotic groups and compared them with saline. Magann 1993 used a factorial design to also assess skin preparation regimens; we combined arms as appropriate. Dashow 1986 was a five‐arm trial assessing saline and four different antibiotic solutions; we combined the antibiotic groups here. Comparisons between the different antibiotics are assessed in comparison 5. Antibiotics used included: gentamicin, clindamycin (alone or in combination), ampicillin, tetracycline, cefotetan, cephapirin or cefoxitin, cefazolin, kanamycin, epicillin or lincomycine, cephalothin, chloramphenicol, cefamandole and moxalactam. Doses and concentrations of both antibiotics and antiseptics varied; full details are given in Characteristics of included studies . Bourgeois 1985 ; Oleson 1980 and Tighe 1982 were three‐arm studies that also randomised participants to no irrigation; these groups are included in comparison 1. In one case we were unsure whether two study reports included some of the same participants ( Chang 2006 ; Cheng 2005 ). Attempts to contact the authors for clarification were unsuccessful so we have included only data from the larger of the two studies ( Cheng 2005 ) in our an analysis for the primary outcome of SSI and conducted a sensitivity analysis to explore the impact of including both data sets independently; only one of these studies reported secondary outcomes so the issue did not impact these analyses. Thirty‐one studies (5141 randomised participants) reported analysable data for the outcome of SSI, which was variously defined (some studies did not provide a definition) ( Al‐Shehri 1994 ; Baker 1994 ; Carl 2000 ; Case 1987 ; Chang 2006 ; Cheng 2005 ; Dashow 1986 ; Greig 1987 ; Halsall 1981 ; Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ; Levin 1983 ; Lord 1983 ; Magann 1993 ; Mirsharifi 2008 ; Moylan 1968 ; Neeff 2016 ; Oestreicher 1989 ; Oleson 1980 ; Oller 2015 ; Rambo 1972 ; Ruiz‐Tovar 2011 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Schein 1990 ; Silverman 1986 ; Sindelar 1979 ; Takesue 2011 ; Vallance 1985 ). Details for all studies are given in Table 5 . However, Chang 2006 was included only for a sensitivity analysis (see below). Two studies ( Marti 1979 ; Tighe 1982 ) reported data which could not be included in the analysis as events were not attributable to groups. There may be, on average, a benefit to the use of some form of antibacterial irrigation compared with non‐antibacterial irrigation. The pooled RR for SSI was 0.57 (95% CI 0.44 to 0.75; I 2 = 53%) Analysis 2.1 . This was low‐certainty evidence downgraded once because 54% of the analysis weight was contributed by studies at high risk of bias in one or more domains, and once because publication bias was considered likely to have affected the result ( Figure 5 ). We conducted an exploratory post‐hoc Egger test on the advice of peer‐reviewers. The P value for small study effects was 0.073. The RR equates to an absolute difference in risk of 60 (95% CI 35 to 78) fewer SSIs per 1000 participants with antibacterial irrigation than with non‐antibacterial irrigation. Funnel plot of comparison 2: antibacterial versus non‐antibacterial irrigation, outcome: 2.1 surgical site infection We also undertook planned subgroup analysis based on the category of surgery. Because only one study that we classed as contaminated reported analysable data, we grouped this together with the studies of dirty or mixed surgical populations. The estimates of effect for the groups were as follows: clean RR 0.16 (95% CI 0.03 to 0.89); clean‐contaminated RR 0.57 (95% CI 0.40 to 0.79) and contaminated, dirty or mixed RR 0.61 (95% CI 0.40 to 0.92). It was not clear that these subgroupings explained much of the heterogeneity between studies; the I 2 for between‐group differences was 9.7%. The result for the clean subgroup is fragile as it is based on very low event rates in small studies, with a zero event rate in one intervention group. We did not carry out planned subgroup analysis for the comparison of antibacterial and non‐antibacterial irrigants for adults and children; only three studies ( Kokavec 2008 ; Kubota 1999 ; Kubota 2015 ), representing 3% of the analysis weight, enrolled only children, so meaningful results were unlikely. One of these studies enrolled children undergoing clean, orthopaedic surgeries ( Kokavec 2008 ); this reported 0 out of 79 participants with SSI in the antibacterial group compared with 2 out of 83 in the non‐antibacterial group. The other two studies ( Kubota 1999 ; Kubota 2015 ) enrolled children undergoing surgeries for appendicitis, classed as dirty. The two studies reported a total of 1 out of 32 participants with SSI in the antibacterial groups compared with 8 out of 28 in the non‐antibacterial group; both studies were at high risk of bias in one domain. We undertook an exploratory post‐hoc subgroup analysis of the type of antibacterial irrigation (antiseptic or antibiotic) to test the rationale for combining all studies comparing irrigation with no irrigation in the same comparison. This analysis did not explain the heterogeneity, supporting the analysis plan employed, also based on clinical assessment. The results of this exploratory analysis are shown in Table 6 . As noted we were unsure whether two study reports included some of the same participants ( Chang 2006 ; Cheng 2005 ). Attempts to contact the study authors for clarification were unsuccessful so we have included only data from the larger of the two studies ( Cheng 2005 ) in our an analysis. A sensitivity analysis to explore the impact of including both data sets independently did not materially change the estimate of effect (RR 0.56, 95% CI 0.43 to 0.74; I 2 = 51%). We conducted a planned sensitivity analysis to look at the impact of excluding studies at high risk of bias in one or more domains. This had the effect of excluding half of the studies and the majority of participants with reported data and produced a larger estimate of effect than the main analysis (RR 0.38 95% CI 0.25 to 0.58). Because so many participants were excluded we do not place any emphasis on this analysis. No studies were at high risk of detection bias so we did not perform this planned sensitivity analysis. Three studies ( Case 1987 ; Chang 2006 ; Takesue 2011 ) with 660 participants reported wound dehiscence and the impact of antibacterial irrigation on dehiscence is very uncertain (RR 1.26; 95% CI 0.65 to 2.45, I 2 = 0%) Analysis 2.2 . This was very low‐certainty evidence downgraded once for risk of bias in the study with the great majority of weight in the analysis, once for imprecision and once for inconsistency. Three studies with 202 participants reported analysable data on overall adverse events that could be clearly determined to represent all participants with an adverse event ( Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016b ; Schein 1990 ). There is no clear difference between the groups (RR 0.55, 95% CI 0.22 to 1.34, I 2 = 0%; 178 participants); this was low‐certainty evidence downgraded twice for imprecision Analysis 2.3 . Ten studies focused specifically on abscess formation, which we had prespecified as a specific event of interest ( Al‐Shehri 1994 ; Baker 1994 ; Dashow 1986 ; Kubota 1999 ; Kubota 2015 ; Oleson 1980 ; Rambo 1972 ; Ruiz‐Tovar 2012 ; Schein 1990 ; Silverman 1986 ). Rambo 1972 grouped abscesses together with another type of event so could not be included in the analysis. Therefore nine studies were included in the analysis, three of which reported no events in either arm ( Al‐Shehri 1994 ; Dashow 1986 ; Oleson 1980 ). It is uncertain whether there is a difference in abscess formation between antibacterial and non‐antibacterial irrigation; the pooled RR was 0.82, 95% CI 0.42 to 1.62, I 2 = 0%; 1309 participants); this is very low‐certainty evidence downgraded once for risk of bias and twice for imprecision Analysis 2.4 . A further eight studies reported additional specific types of adverse events that we had not prespecified, such as respiratory distress or endometritis, or made general non‐group specific statements about events ( Bourgeois 1985 ; Levin 1983 ; Lord 1983 ; Magann 1993 ; Marti 1979 ; Moylan 1968 ; Ruiz‐Tovar 2016a ; Silverman 1986 ); several of the studies included in analyses of abscess also specified such events. Details are provided in Characteristics of included studies but these data are not further analysed. Eleven studies (1121 participants) reported data on mortality for antibacterial vs. non‐antibacterial irrigation ( Baker 1994 ; Browne 1978 ; Lord 1983 ; Oller 2015 ; Rambo 1972 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Ruiz‐Tovar 2016b ; Schein 1990 ; Vallance 1985 ). It is uncertain whether there is a difference in mortality between the treatment groups (RR 0.81, 95% CI 0.48 to 1.36) Analysis 2.5 . This was very low‐certainty evidence downgraded once for risk of bias in studies contributing 64% of the weight in the analysis and twice for imprecision. Fifteen studies reported some data on length of hospital stay ( Al‐Shehri 1994 ; Baker 1994 ; Bourgeois 1985 ; Halsall 1981 ; Kubota 1999 ; Kubota 2015 ; Levin 1983 ; Oleson 1980 ; Oller 2015 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ; Schein 1990 ; Tighe 1982 ; Vallance 1985 ). Three studies did not report data separately for the intervention groups ( Al‐Shehri 1994 ; Baker 1994 ; Tighe 1982 ). Seven studies reported mean length of stay although two ( Halsall 1981 ; Schein 1990 ) did not report measures of variance. There may, on average, be a very slightly shorter length of stay in participants treated with antibacterial irrigation. The difference in means was ‐0.85 days (95% CI ‐1.60 to ‐0.09; I 2 = 55%; 635 participants) Analysis 2.6 . Five studies reported median length of stay ( Oleson 1980 ; Oller 2015 ; Ruiz‐Tovar 2012 ; Ruiz‐Tovar 2013 ; Ruiz‐Tovar 2016a ); in each case the median lengths of stay were very similar for the two groups. This was low‐certainty evidence downgraded for risks of bias across multiple domains. Two studies with a total of 375 participants reported some data on use of systemic antibiotics ( Chang 2006 ; Tighe 1982 ). Tighe 1982 did not report the data based on treatment group allocation (they noted 53 of 131 participants receiving antibiotics "distributed evenly across the groups"); while Chang 2006 reported that all six of the participants with SSI received systemic antibiotics up to six weeks postoperatively (there were no infections in the povidone iodine group). Calculating an RR for this outcome would not produce a meaningful result since the data merely duplicate the results for the primary outcome of SSI; consequently no independent GRADE assessment is possible. Five studies with 1198 participants reported some information about antibiotic resistance in organisms sampled ( Chang 2006 ; Lord 1983 ; Moylan 1968 ; Rambo 1972 ; Takesue 2011 ). Chang 2006 reported that 5 out of 6 infections in participants treated with saline tested positive for methicillin‐resistant Staphylococcus aureus (MRSA) (there were no infections in the povidone iodine group). Takesue 2011 also focused on S. Aureus resistance and reported data for a majority of the participants with infection; however, the data could not be linked to the proportion of participants with or without resistance. Both studies used antiseptic rather than antibiotic irrigations. Moylan 1968 reported tests for resistance to kanamycin (the antibiotic used in the study) in all wound cultures but provided specific results on the proportion with resistance for only one group. Lord 1983 and Rambo 1972 reported data for resistance for specific organisms but these data were incomplete and could not be linked to participant‐level infections. We were not able to calculate any meaningful estimate of effect for the proportion of participants with antibiotic‐resistant infection and therefore no GRADE assessment was possible. Two studies with 403 participants reported data on reoperation ( Chang 2006 ; Silverman 1986 ). There were low numbers of events. It is uncertain if there is a difference between the treatment groups. The RR was 1.26 (95% CI 0.12 to 13.60) Analysis 2.7 . This was very low‐certainty evidence downgraded once for inconsistency and twice for imprecision. No study reported on readmission to hospital. Thirty‐six studies compared irrigation with antibacterial and non‐antibacterial irrigants and 33 reported the outcome of SSI; data from 30 studies with over 5000 participants could be included in the analysis. There may be a lower incidence of SSI in participants treated with antibacterial irrigation solutions compared with non‐antibacterial irrigants. This was low‐certainty evidence downgraded once for risk of bias in varying domains affecting studies that account for over half the weight of the analysis and once because publication bias is suspected. A pre‐planned subgroup analysis showed that the possible benefit was present in each of the surgical contamination subgroups that we were able to assess (clean versus clean‐contaminated versus contaminated or dirty) although the results in the clean group were based on small numbers of participants and very low numbers of events. Exploratory subgroup analysis confirmed that it was reasonable to combine different types of antibacterial solution in a single analysis. It is very uncertain whether there is a difference in the incidence of wound dehiscence between the treatment groups; this was very low‐certainty evidence based on three studies. Table 4 One study (20 participants) compared irrigating with saline and artifical cerebrospinal fluid (CSF) in 20 participants undergoing clipping of cerebral aneurysms (classed as clean) ( Shimizu 2011 ). Two studies compared irrigation with icodextrin and Ringer's solution. One enrolled 426 women undergoing primary removal of myomas or endometriotic cysts ( Trew 2011 ); a second study enrolled 449 women undergoing laparoscopic gynaecological surgery for a range of diagnoses ( Brown 2007 ). Both these studies involved surgeries classed as clean‐contaminated. Shimizu 2011 did not report SSI. The RR for Trew 2011 was 2.89 (95% CI 0.30 to 27.56; 426 participants). In Brown 2007 it was not clear that the infection data reported referred to SSI; attempts to clarify this with the study authors have not been successful so far. There is no clear evidence of a difference. This was low‐certainty evidence downgraded twice for imprecision based only on the data from the trial where we were confident this was SSI data ( Trew 2011 ). This was not reported by either study. Both Brown 2007 and Trew 2011 reported no deaths in either intervention group (total of 875 participants). Since no estimate of effect was therefore calculable no full GRADE assessment was made; the evidence is affected by imprecision however Analysis 3.1 . Shimizu 2011 reported the number of participants with postoperative events; this included neurological events and events visualised on CT or MRI scans. There were two participants with events in each group (total of 20 participants); because of the inclusion of imaging results in these data we have not reported an effect estimate and have not undertaken a GRADE assessment. Both Brown 2007 and Trew 2011 reported total number of participants with adverse events and the number with events that were considered to be related to treatment. There was, on average, no difference in the number of participants with an adverse event (RR 0.99, 95% CI 0.96, 1.02; I 2 = 0%; 875 participants) Analysis 3.2 . The effect estimate for events considered to be related to treatment may be a more meaningful measure; this also showed no clear difference, on average, with confidence intervals that included the possibility of a small benefit from icodextrin as well as harm: RR 1.35 (95% CI 0.98 to 1.86; I 2 = 0%; 875 participants) Analysis 3.3 . This was moderate‐certainty evidence downgraded once for imprecision. Brown 2007 also reported the proportions of participants with serious adverse events (RR 1.20, 95% CI 0.80 to 1.78; 426 participants) and serious events that were considered to be treatment‐related (RR 0.71, 95% CI 0.29 to 1.73; 449 participants). In both cases there may be little or no difference between the treatment groups (low‐certainty evidence). No studies reported data for other secondary outcomes. There were two comparisons where both arms involved a solution without antibacterial properties. A single study comparing saline with artifical CSF in brain surgery (clean) did not report either SSI or wound dehiscence. Two studies compared icodextrin with Ringer's solution in gynaecological surgery (clean‐contaminated) but only one clearly reported SSI and neither reported wound dehiscence. There is no clear difference in SSI incidence between the treatment groups. This was low‐certainty evidence downgraded twice for imprecision. Table 4 One study compared povidone iodine with superoxidised water irrigation (Dermacyn) in 190 participants undergoing coronary artery bypass graft (CABG) (classed as clean) ( Mohd 2010 ). One three‐armed study compared povidone iodine with chlorhexidine in 53 adults undergoing surgery for peritonitis (classed as dirty) ( Vallance 1985 ); a third group were randomised to saline irrigation (see comparison 2). The number of participants relevant to this comparison was 33. There may be more infections in wounds irrigated with povidone iodine compared with Dermacyn. The RR for Mohd 2010 was 2.80 (95% CI 1.05 to 7.47; 190 participants). This would represent an absolute difference of 95 more SSIs per 1000 people treated with povidone iodine than with superoxidised water (95% CI 3 more to 341 more). This was low‐certainty evidence downgraded once for risk of bias and once for imprecision. It is uncertain whether there is a difference between the groups. The RR in Vallance 1985 was 1.13 (95% CI 0.78 to 1.63; 29 participants). This represents a completed case analysis, as early mortality cases were excluded from the analysis and could not be accurately assigned to groups. This was very low‐certainty evidence downgraded twice for risks of bias across multiple domains and twice for imprecision. Details for both studies are given in Table 5 ; GRADE judgements are summarised in Table 4 . This was not reported by any of the studies. Mohd 2010 reported deaths together with the need for reopening of the chest due to bleeding. There were four deaths in total but it was not clear in which group they occurred. A full GRADE assessment was not possible but certainty would be affected by risk of bias as well as imprecision. It is uncertain whether there is a difference between the groups. The RR in Vallance 1985 was 0.45 (0.05 to 3.90; 33 participants). These data refer to deaths within four days of surgery; later mortality was recorded but was not reported separately for the treatment groups. This was very low‐certainty evidence downgraded twice for risks of bias across multiple domains and twice for imprecision. It is uncertain whether there is a difference between the groups.The difference in means in Vallance 1985 was 3.30 days more in the povidone iodine group (95% CI 0.53 to 6.07; 33 participants). This was very low‐certainty evidence downgraded twice for risks of bias across multiple domains and twice for imprecision. It is uncertain whether there is a difference between the groups. The RR in Mohd 2010 was 8.80 (95% CI 0.48 to 161.11; 178 participants) based on four events, all in the povidone iodine group. This was very low‐certainty evidence downgraded once for risk of bias and twice for imprecision. No studies reported data for other secondary outcomes. There were two studies where one arm was povidone iodine and the other was another antiseptic solution. Each study undertook a different comparison. Numbers of participants were low. The comparison with superoxidised water (Dermacyn) was undertaken in clean cardiac operations while the comparison with chlorhexidine was in dirty operations for peritonitis. There may be more infections in wounds treated with povidone iodine compared with superoxidised water; low‐certainty evidence downgraded once for risk of bias and once for imprecision. It is very uncertain whether there is a difference in SSI incidence between povidone iodine and chlorhexidine; very low‐certainty evidence downgraded twice for risk of bias across multiple domains and twice for imprecision. Neither study reported wound dehiscence. Table 4 One three‐arm study compared use of cephapirin with cefoxitin in 132 women undergoing caesarean sections (classed as clean‐contaminated) ( Levin 1983 ); a third group were randomised to saline irrigation (see comparison 2). The number of participants relevant to this comparison was 85. One three‐arm study compared the use of clindamycin with gentamicin in 51 women undergoing planned axillary node dissection ( Oller 2015 ); a third group of women were randomised to saline (see comparison 2). The number of participants relevant to this comparison was 34. All participants received an initial saline irrigation, women in the two antibiotic groups received a second irrigation with either gentamicin or clindamycin solution. This surgery was classed as clean. One three‐arm study compared the use of epicillin with lincomycine in a group of 162 adults and children undergoing surgery for appendicitis (classed as contaminated) ( Marti 1979 ); a third group of participants were randomised to saline irrigation (see comparison 2). One five‐arm study assessed irrigation with four different antibiotic solutions (cephapirin, cefamandole, moxalactam or ampicillin) or saline in 360 women undergoing caesarean section ( Dashow 1986 ). The comparison of antibiotic irrigation versus saline is included in comparison 2; we were also able to assess six comparisons involving the individual antibiotics. One study assessed irrigation with either cefazolin of cefamandole in women undergoing caesarean section. Peterson 1990 enrolled 207 women and randomised 113 to groups relevant to this review. The RR for Levin 1983 was not estimable because there were no SSI events in either treatment group (85 participants). Therefore no full GRADE assessment was possible but the certainty of the evidence would be affected by risks of bias as well as imprecision. Marti 1979 did not specify the number of participants relevant to this comparison (162 total participants) and did not report any outcome data by the intervention group in which the event occurred, instead reporting only the total number of events in all three intervention groups for both SSI and adverse events. We could not analyse these data further and no full GRADE assessment was possible, but the certainty of the evidence would be affected by risks of bias as well as imprecision. The RR for Oller 2015 was not estimable because there were no SSI events in either treatment group (34 participants relevant to this comparison). Therefore no full GRADE assessment was possible; the certainty of this evidence would be affected by imprecision. The RR for Dashow 1986 was 1.37 (95% CI 0.24 to 7.95; 134 participants) based on 3 out of70 participants with SSI in the cephapirin group and 2 out of 64 in the cefamandole group. The RR for Dashow 1986 was 1.69 (95% CI 0.29 to 9.84; 149 participants) based on 3 out of 70 participants with SSI in the cephapirin group and 2 out of 79 in the moxalactam group. The RR for Dashow 1986 was 7.00 (95% CI 0.37 to 133.06; 140 participants) based on 3 out of 70 participants with SSI in the cephapirin group and 0 out of 70 in the ampicillin group. The RR for Dashow 1986 was 1.23 (95% CI 0.18 to 8.52; 143 participants) based on 2 out of 64 participants with SSI in the cefamandole group and 2 out of 79 in the moxalactam group. The RR for Dashow 1986 was 5.46 (95% CI 0.27 to 111.65; 134 participants) based on 2 out of 64 participants with SSI in the cefamandole group and 0 out of 70 in the ampicillin group. The RR for Dashow 1986 was 4.44 (95% CI 0.22 to 90.88; 149 participants) based on 2 out of 79 participants with SSI in the moxalactam group and 0 out of 70 in the ampicillin group. The RR for ( Peterson 1990 ) was 4.58 (95% CI 0.22 to 93.38; 113 participants) based on 2 out of 59 participants with SSI in the cefazolin group and 0 out of 54 in the cefamandole group. Where a full GRADE assessment was possible, in each case we judged these estimates to represent low‐certainty evidence, which was downgraded twice for serious imprecision. Details for all studies are given in Table 5 ; GRADE judgements are summarised in Table 4 . This was not reported by any of the studies. Levin 1983 reported only a single type of adverse event (endometritis); these data were not further analysed. Marti 1979 reported that one abscess occurred in the groups treated with antibiotics but did not report in which group the event occurred therefore no full GRADE assessment was possible although the certainty of the evidence would be affected by risks of bias as well as imprecision. Dashow 1986 reported that there were no occurrences of abscess in any group; because there were zero events in every group (total 360 participants), no estimates of effect could be calculated for any comparison. The study also reported the proportion of participants with infection‐related morbidity; these data did not clearly represent all participants with adverse events and were not further analysed for any of the six comparisons of antibiotics. No full GRADE assessment was possible for any of the comparisons but any assessment of the certainty of the evidence would be affected by imprecision. The RR for Oller 2015 was not estimable because there were no events in either treatment group (34 participants relevant to this comparison). Therefore no GRADE assessment was possible. No other studies reported this outcome. There may be little or no difference between the groups; the difference in means in Levin 1983 was 0.10 days (lower for the cephapirin group) (95% CI ‐0.78 to 0.58; 85 participants). This was low‐certainty evidence downgraded twice for imprecision. Oller 2015 reported a median length of stay of 3 days (range 1 to 3) in each group (total 34 relevant participants) suggesting that there may be little difference between the groups. This was low‐certainty evidence downgraded twice for imprecision. No other studies reported this outcome. No studies reported data for other secondary outcomes. There were 10 comparisons of different antibiotic solutions. Each comparison was assessed in a single study; six comparisons were represented by the same trial that randomised participants to saline or one of four different antibiotic solutions. Numbers of participants were low. All of the comparisons reported SSI as an outcome and none reported wound dehiscence. For three comparisons we could not calculate an estimate of effect, either because there were no events (cephapirin versus cefoxitin and clindamycin versus gentamicin) or because no group data were reported (epicillin versus lincomycine). In each of the other comparisons (cephapirin versus cefamandole; cephapirin versus moxalactam; cephapirin versus ampicillin; cefamandole versus moxalactam; cefamandole versus ampicillin; moxalactam versus ampicillin; cefazolin versus cefamandole) there was low‐certainty evidence of no clear difference between the groups, downgraded twice for imprecision because of wide confidence intervals, which included the possibility of no effect and both benefit and harm for each treatment. All except the last of these comparisons were represented by the single, multi‐arm trial. Although all classes of surgery were represented, effect estimates were only calculable for those comparisons assessed in clean‐contaminated surgery. Table 3 Comparison of standard (non‐pulsed) saline irrigation using a jug or a syringe with pulsatile saline irrigation was assessed by two studies ( Hargrove 2006 ; Nikfarjam 2014 ) with a total of 484 participants. Hargrove 2006 enrolled 356 people (ages not reported clearly) having surgery for displaced neck of femur (classed as clean). Nikfarjam 2014 enrolled 137 adults undergoing open elective abdominal surgery scheduled to last at least two hours (classed as clean‐contaminated). Both Hargrove 2006 and Nikfarjam 2014 assessed SSI. There may, on average, be a lower incidence of SSI in participants treated with pulsatile irrigation compared with standard irrigation. There were 13 cases of SSI in the 230 participants in the pulsatile groups compared with 42 out of 254 in the standard groups. The pooled RR was 0.34 (95% CI 0.19, 0.62; I 2 = 0%; 484 participants) Analysis 4.1 . This was low‐certainty evidence, which was downgraded twice for multiple additional risks of bias in Hargrove 2006 , which contributed 69% of the weight in the analysis; both studies were necessarily at high risk of performance bias due to the nature of the comparison. The RR equates to an absolute risk difference of 109 (95% CI 62 to 134) fewer SSIs per 1000 participants with pulsatile irrigation than with standard irrigation. Because there was only a single study in each surgical class and populations were mixed or adult we were unable to conduct pre‐planned subgroup analyses on the basis of either surgical category or adult/paediatric populations. Nikfarjam 2014 reported that there was one incidence of wound dehiscence in the standard irrigation group. The RR for this was 0.31 (95% CI 0.01 to 7.55; 128 participants). This was low‐certainty evidence downgraded twice for imprecision. Hargrove 2006 reported that there were 25 deaths among the 356 participants but did not state in which treatment group they occurred; Nikfarjam 2014 did not report mortality. No GRADE assessment was possible. Nikfarjam 2014 reported the number of participants with complications that were not wound infections. The RR was 1.31 (95% CI 0.87 to 1.97; 128 participants). This was low‐certainty evidence downgraded twice for imprecision. Nikfarjam 2014 reported that 14 of the 16 participants with wound infection were treated with systemic antibiotics but did not report data by treatment group; no GRADE assessment was possible. Hargrove 2006 reported that "half" of the wound infections tested positive for MRSA but did not report data by treatment group. Nikfarjam 2014 reported some qualitative data on the organisms isolated. No GRADE assessment was possible. Nikfarjam 2014 reported the median length of stay as 9 days in both groups, the range in the pulsatile group was 5 to 45 days compared with 4 to 71 days in the standard group. This suggested that there may be little difference between the groups. This was moderate‐certainty evidence downgraded once for imprecision. Nikfarjam 2014 reported the need for reoperation for two specific reasons: major debridement and relaparotomy. The effect estimate for all reintervention showed no clear difference between the groups (RR 0.56, 95% CI 0.14 to 2.26; 128 participants). This was low‐certainty evidence downgraded twice for imprecision. Nikfarjam 2014 reported readmissions to hospital; there is no clear difference between the groups. The RR was 1.41 (95% CI 0.53 to 3.73; 128 participants). This was low‐certainty evidence downgraded twice for imprecision. Two studies assessed pulsatile versus standard techniques of irrigation using saline. One was conducted in clean and one in clean‐contaminated surgeries. There may be fewer incidences of SSI in participants treated with pulsatile irrigation compared with normal irrigation. This was low‐certainty evidence downgraded twice for multiple additional risks of bias in the study with the majority of the weight in the analysis; both studies were also at high risk of performance bias. There is no clear difference between the groups in the incidence of wound dehiscence; low‐certainty evidence downgraded twice for imprecision.

1 Downgraded once for risk of bias in one or more domains other than performance bias in studies that account for more than 50% of the analysis weight; downgraded once for imprecision because confidence intervals include both benefit and harm. Publication bias could not be clearly ruled out but was not additionally downgraded for as the evidence was unclear.
 2 Downgraded twice for imprecision because confidence intervals are wide and fragile and include the possibility of both benefit and harm. There is also uncertainty as to whether the analysis was correctly adjusted for a split‐body design.
 3 Downgraded once for imprecision and once for high risk of detection bias in the study with 77% of the analysis weight.
 4 Downgraded once for imprecision. 1 Downgraded once for risk of bias due to high risk of bias for at least one domain in studies contributing over 50% of the weight and once for probable publication bias. We did not further downgrade for inconsistency because the inconsistency present appeared due to the difference between larger and smaller studies and hence was accounted for by the downgrade for potential publication bias.
 2 Downgraded once for inconsistency due to study with highest weight showing effect in opposite direction to other included studies, once for high risk of bias and twice for imprecision, due to confidence intervals being wide and fragile, and including both benefit and harm.
 3 Downgraded twice for imprecision due to wide and fragile confidence intervals, which included both benefit and harm, as well as no difference between interventions.
 4 Downgraded once for risk of bias in studies with the majority of the weight and twice for imprecision due to wide and fragile confidence intervals, which included both benefit and harm, as well as no difference between interventions. 1 Downgraded twice for high risk of bias in multiple domains for study contributing most of the weight.
 2 Downgraded twice for imprecision due to wide and fragile confidence intervals, which include both benefit and harm.

Implications for practice The evidence base identified by this review was generally of low certainty, which means that the true effects may be substantially different to the estimates of effect. Therefore where we have identified a difference in surgical site infection (SSI) incidence ‐ as with the comparisons of antibacterial and non‐antibacterial interventions and pulsatile versus standard methods ‐ these should be considered in the context of uncertainty. This is particularly the case as we suspect that the evidence base may have been affected by the tendency for small studies with negative results to remain unpublished and absent from meta‐analyses. Clinicians should also consider whether the evidence is relevant to the surgical populations under consideration, for instance where the surgery is considered to be a clean procedure. They should also take into consideration the limited data available on wound dehiscence. They may also wish to consider the varying reporting of prophylactic antibiotic use delivered by other means (e.g. oral, intramuscular etc); in some of the studies in the review no such prophylaxis was reported whereas their practice may be to routinely use this for the procedure under consideration ‐ or vice‐versa. They may wish to consider this in conjunction with the evidence of this review on the efficacy of different types of irrigation solutions. The limited reporting of many relevant outcomes should also be considered. Finally, while many studies in the review are recent, others are old and predate current levels of, and concern over, the development of antibiotic resistance. The evidence base identified by this review was generally of low certainty, which means that the true effects may be substantially different to the estimates of effect. Therefore where we have identified a difference in surgical site infection (SSI) incidence ‐ as with the comparisons of antibacterial and non‐antibacterial interventions and pulsatile versus standard methods ‐ these should be considered in the context of uncertainty. This is particularly the case as we suspect that the evidence base may have been affected by the tendency for small studies with negative results to remain unpublished and absent from meta‐analyses. Clinicians should also consider whether the evidence is relevant to the surgical populations under consideration, for instance where the surgery is considered to be a clean procedure. They should also take into consideration the limited data available on wound dehiscence. They may also wish to consider the varying reporting of prophylactic antibiotic use delivered by other means (e.g. oral, intramuscular etc); in some of the studies in the review no such prophylaxis was reported whereas their practice may be to routinely use this for the procedure under consideration ‐ or vice‐versa. They may wish to consider this in conjunction with the evidence of this review on the efficacy of different types of irrigation solutions. The limited reporting of many relevant outcomes should also be considered. Finally, while many studies in the review are recent, others are old and predate current levels of, and concern over, the development of antibiotic resistance. Implications for research We did not identify any trials that compared antibiotic irrigation with antiseptic irrigation; this represents a gap in the direct evidence base, which may merit further investigation. If the possible benefit of antibacterial irrigation treatment represents a true effect this is particularly worth investigating, given growing concerns over antibiotic resistance. The evidence base we have identified means that this gap in the evidence could be investigated using a network meta‐analysis; an analysis of the indirect evidence for the comparison could then inform a decision as to whether new primary research was warranted. There was a considerable amount of heterogeneity between the studies we identified and this was not explicable by surgery class in prespecified analyses. Exploratory analyses also confirmed that this was not explained by our decision to combine studies using different types of irrigation fluids. We did not pre‐specify the operative point of irrigation as being a factor of interest (i.e. at what level of wound closure it was undertaken); this did vary between studies and is a factor that may benefit from investigation. Future trials should also carefully consider how prophylactic antibiotics would be used and documented. Any future network analysis could also consider indirect evidence for comparisons of different volumes of particular solutions. Any further research, whether primary or secondary should also take account of the level of contamination of procedures under consideration although we have not identified this as an effect modifier. Finally pulsatile irrigation should be explored further in primary research. The authors of one of the included studies Nikfarjam 2014 suggest that pulsatile irrigation may reduce bacterial counts and help to remove tissue that could otherwise act as a focus for infection but the mechanism for its possible benefit is not clear and would require further research. Any new primary research should use this systematic review and meta‐analysis as a guide for calculating sample sizes, in order to have sufficient power to detect a difference in SSIs, particularly if undertaken in participants undergoing clean or clean‐contaminated surgery where event rates are low. Any such trial should use appropriate and robust research methodology to reduce the risks of bias, should use internationally recognised criteria for the diagnosis of SSI and should have adequate follow‐up procedures and duration to ensure that SSIs occurring after hospital are recorded. Other outcomes such as wound dehiscence ‐ a primary review outcome for which there was little evidence ‐ and health‐related quality of life should also be considered. In view of the limited reporting of relevant outcomes that this review has identified, consideration should be given to the development and use of core outcome sets defined using transparent and rigorous methodology. We identified a number of ongoing trials and the completion dates of these should be taken into consideration in the planning of a network meta‐analysis. We did not identify any trials that compared antibiotic irrigation with antiseptic irrigation; this represents a gap in the direct evidence base, which may merit further investigation. If the possible benefit of antibacterial irrigation treatment represents a true effect this is particularly worth investigating, given growing concerns over antibiotic resistance. The evidence base we have identified means that this gap in the evidence could be investigated using a network meta‐analysis; an analysis of the indirect evidence for the comparison could then inform a decision as to whether new primary research was warranted. There was a considerable amount of heterogeneity between the studies we identified and this was not explicable by surgery class in prespecified analyses. Exploratory analyses also confirmed that this was not explained by our decision to combine studies using different types of irrigation fluids. We did not pre‐specify the operative point of irrigation as being a factor of interest (i.e. at what level of wound closure it was undertaken); this did vary between studies and is a factor that may benefit from investigation. Future trials should also carefully consider how prophylactic antibiotics would be used and documented. Any future network analysis could also consider indirect evidence for comparisons of different volumes of particular solutions. Any further research, whether primary or secondary should also take account of the level of contamination of procedures under consideration although we have not identified this as an effect modifier. Finally pulsatile irrigation should be explored further in primary research. The authors of one of the included studies Nikfarjam 2014 suggest that pulsatile irrigation may reduce bacterial counts and help to remove tissue that could otherwise act as a focus for infection but the mechanism for its possible benefit is not clear and would require further research. Any new primary research should use this systematic review and meta‐analysis as a guide for calculating sample sizes, in order to have sufficient power to detect a difference in SSIs, particularly if undertaken in participants undergoing clean or clean‐contaminated surgery where event rates are low. Any such trial should use appropriate and robust research methodology to reduce the risks of bias, should use internationally recognised criteria for the diagnosis of SSI and should have adequate follow‐up procedures and duration to ensure that SSIs occurring after hospital are recorded. Other outcomes such as wound dehiscence ‐ a primary review outcome for which there was little evidence ‐ and health‐related quality of life should also be considered. In view of the limited reporting of relevant outcomes that this review has identified, consideration should be given to the development and use of core outcome sets defined using transparent and rigorous methodology. We identified a number of ongoing trials and the completion dates of these should be taken into consideration in the planning of a network meta‐analysis.

Surgical site infections (SSIs) encompass a range of superficial to deep wound infections that can occur after an operative procedure. SSIs are a preventable complication, responsible for substantial financial burden to health services that can result in poorer patient outcomes, increased mortality, morbidity and reoperation rates. A 2006 prevalence survey in the UK National Health Service (NHS) indicated that approximately 8% of all patients (5743/75,694 patients over a four‐month period) admitted to hospital suffer healthcare‐associated infections, with 15% of these infections being SSIs ( Smyth 2008 ). A US study found that in over 750,000 episodes of surgical hospitalisation, 1% resulted in a SSI, and similar estimates have been found in France ( Astagneau 2009 ; De Lissovoy 2009 ). However, such values are known to underestimate the levels of SSI by not considering those that develop outside hospitals ( Bruce 2001 ; Gibbons 2011 ), as most SSIs present within the first 30 days following a procedure, although commonly between the fifth and tenth postoperative day ( NICE 2008 ). Patients who develop SSIs have longer hospital stays and incur higher treatment costs than other patients; in some types of surgery they also have higher mortality rates ( Coello 2005 ; Jenks 2014 ). Diagnosis with a SSI after hospital discharge is associated with a greater number of healthcare visits, higher resource use, and more readmissions ( Perencevich 2003 ). While more data are available for Western healthcare settings, SSI was the leading cause of hospital‐acquired infection in a systematic review of studies in low‐ and middle‐income countries ( Allegranzi 2010 ). Surgical site infection can also contribute to wound dehiscence, which is also a primary outcome of this review; such wounds may then convert to healing by secondary intention with a resultant increased healing time and impact on the individual and on costs to the health service. While the cause of SSIs is multifactorial, recognised risk factors include: length of hospital stay, obesity, patient co morbidities, duration and complexity of surgery, and degree of wound contamination ( Anderson 2008 ; Chemaly 2010 ; Edwards 2008 ; Korol 2013 ; Omran 2007 ). Using the classification system adopted by the Centers for Disease Control and Prevention (CDC; HICPAC 1999 ), wounds can be classified by their level of contamination as follows. Clean (Class 1): noninfective operative wounds in which no inflammation is encountered, with no involvement of respiratory, gastrointestinal, genitourinary tract, and oropharyngeal cavity. Clean‐contaminated (Class 2): operative wounds in which either the respiratory, gastrointestinal, or genitourinary tract is entered under controlled conditions and with only minor contamination. This category specifically includes wounds as a result of operations involving the biliary tract, appendix, and oropharynx, provided no evidence of infection or a major break in sterile technique is encountered. Contaminated (Class 3): fresh, accidental wounds, resulting from operations with major breaks in sterile technique or gross spillage from the gastrointestinal tract, and incisions in which acute, nonpurulent (free from pus) inflammation is encountered. This category includes traumatic lacerations. Dirty (Class 4): old traumatic wounds with retained devitalised tissue and those that involve existing clinical infection or perforated viscera. Organisms causing postoperative infection are likely to be present in the operative field before the operation. Clean (Class 1): noninfective operative wounds in which no inflammation is encountered, with no involvement of respiratory, gastrointestinal, genitourinary tract, and oropharyngeal cavity. Clean‐contaminated (Class 2): operative wounds in which either the respiratory, gastrointestinal, or genitourinary tract is entered under controlled conditions and with only minor contamination. This category specifically includes wounds as a result of operations involving the biliary tract, appendix, and oropharynx, provided no evidence of infection or a major break in sterile technique is encountered. Contaminated (Class 3): fresh, accidental wounds, resulting from operations with major breaks in sterile technique or gross spillage from the gastrointestinal tract, and incisions in which acute, nonpurulent (free from pus) inflammation is encountered. This category includes traumatic lacerations. Dirty (Class 4): old traumatic wounds with retained devitalised tissue and those that involve existing clinical infection or perforated viscera. Organisms causing postoperative infection are likely to be present in the operative field before the operation. The risk of developing a SSI is related to the level of contamination of the wound. Higher classifications of contamination are associated with higher risks of a SSI, as demonstrated in recent surveillance of surgical infections in NHS hospitals in England, which showed that gastrointestinal procedures, especially large bowel surgery, carry the highest risk of bacterial contamination (10.2%) ( Public Health England 2014 ). Conversely, hip and knee prosthesis surgeries were shown to carry the lowest risk of infection, with an occurrence rate of 0.7% and 0.6%, respectively ( Public Health England 2014 ). Standard definitions of SSIs exist, as described by the CDC, the Surgical Site Infection Surveillance Service, the Southampton wound scoring system, and the ASEPSIS score ( Bailey 1992 ; Horan 1992 ; Ridgeway 2005 ; Wilson 1986 ). The most commonly applied definition by the CDC describes three levels of SSI ( Horan 1992 ). The lowest level of SSI can be defined as ' superficial incisional ' infections. These are limited to the skin and subcutaneous tissue. Such infections are identified by localised clinical (Celsian) signs such as redness, pain, heat, swelling, or the drainage of pus. ' Deep incisional' infections affect the fascial and muscular layers and are identified by the presence of pus, abscess, fever, localised tenderness, or the separation of incision edges. Finally, 'cavity space' infection is considered the most severe level of SSI. Such infections can be identified by the drainage of pus, formation of an abscess or histological, radiological, or visual signs during reoperation. These involve anatomical parts of the body that have been manipulated during a surgical procedure, for example, a joint cavity or the peritoneum. Visceral infection is not included within the scope of the CDC guidelines. SSIs are not restricted to these definitions and are often accompanied by microbiological evidence from microscopy and culture of infection tissue and fluid. However, it is important to note that normal flora may colonise superficial skin sites, and therefore positive microbiological growth in the absence of clinical signs is rarely indicative of SSIs. Surgical wound irrigation is an intraoperative surgical technique, which may reduce the rate of SSIs by the removal of debris (dead or damaged tissue), metabolic waste, and wound exudate. It aims to create the optimal environment for wound healing, and is used with variable uptake among surgical practitioners ( Barnes 2014 ). The theoretical advantage of surgical wound irrigation is to reduce the bacterial load in a surgical or traumatic wound by a combination of water pressure, dilution, or the application of antimicrobial agents. Usually, irrigation is undertaken at the end of an operative procedure, prior to wound closure, however postoperative wound irrigation may also be applied. Intracavity lavage is another intraoperative surgical technique, which utilises similar principles to surgical wound irrigation with the aim of reducing SSI risk. It can be adopted during any operation that exposes a bodily cavity, but is most commonly used for procedures on the abdominal (peritoneal) cavity and during joint replacement surgery. Both wound irrigation and intracavity lavage can be altered by three basic variables: volume of irrigation fluid; mechanism/timing of delivery; or solution composition. We use the terms 'irrigation' and 'lavage' separately in this review, however they do not necessarily describe distinctly separate surgical techniques, and may often refer to similar methods of washout for a cavity or a wound. The aim of wound irrigation and lavage is to reduce the bacterial load in a surgical or traumatic wound by a combination of water pressure, dilution, or the application of antimicrobial agents. Usually, this is undertaken at the end of an operative procedure, prior to wound closure, to reduce the likelihood of the introduction of bacteria. Both wound irrigation and intracavity lavage can be achieved using various solutions. Normal saline is commonly used along with antimicrobial agents for intracavity lavage. However, there is concern that antimicrobial agents may damage tissue and prevent normal healing. It is thought that the introduction of large volumes of fluid into a cavity or wound could wash away inflammatory cells vital to the host defence ( Schultz 2011 ). National Institute for Care and Health Excellence (NICE) guidelines reviewed evidence from 20 randomised controlled trials (RCTs) and concluded that the use of surgical wound irrigation or intracavity lavage could not be recommended to reduce the risk of SSIs ( NICE 2008 ). The search used to inform this guideline is now almost 10 years old, making it likely that a number of additional trials will be available. In some areas of surgical practice this is likely to lead to changes in conclusions; we are aware of a recent systematic review which found a benefit to intraoperative irrigation over no irrigation in abdominal surgery ( Mueller 2015 ); this included both RCTs and studies that we consider to be quasi‐RCTs. A recent review restricted to prophylactic wound irrigation (excluding surgeries with high levels of contamination) has just been published ( De Jonge 2017 ), which informed recent WHO guidance ( WHO 2016 ) A recent expert consensus paper also identified the need for more evidence on several of the questions in this review ( Barnes 2014 ). This review aims to update this evidence base.

We identified a total of 59 studies involving 14,738 participants. Most included studies had a parallel‐group design (there was one split‐body design and two factorial designs that assessed, respectively, skin preparation and intravenous antibiotics as well as wound irrigation). Most studies reported the primary review outcome (SSI), with other outcomes of interest sparsely reported. Key results for each comparison and outcome are summarised below. Twenty studies with 7192 participants compared some form of irrigation with no irrigation, The irrigation fluid was either non‐antibacterial (typically saline) or an antiseptic or antibiotic solution. The majority of these studies reported analysable SSI data, which contributed to a pooled analysis, and we were able to carry out one of the prespecified subgroup analyses based on surgical classification. We also undertook an exploratory analysis on the basis of type of irrigation solution, which supported our informed decision to conduct a single analysis that included studies that used different types of irrigation solution. Based on available data there was, on average, no clear difference between the groups in incidence of SSI, and this was also the case in the two subgroups (clean‐contaminated versus contaminated or dirty). This was low‐certainty evidence downgraded for risk of bias and imprecision; although fewer infections were reported in the groups treated with irrigation, confidence intervals included both benefit and harm despite large numbers of participants. Thirty‐six studies (6163 participants) compared a non‐antibacterial (typically saline) irrigation with either an antiseptic (14 studies) or an antibiotic solution (22 studies). The majority of these studies reported analysable SSI data, which contributed to a pooled analysis, and we were able to carry out one of the prespecified subgroup analyses based on surgical classification. We also undertook an exploratory analysis, which confirmed that it was reasonable to conduct a single analysis that included studies that used different types of antibacterial irrigation solution. There may, on average, be a lower incidence of SSI in participants treated with antibacterial irrigation compared with non‐antibacterial irrigation. This was low‐certainty evidence, which was downgraded once due to risk of bias across multiple domains in studies accounting for much of the analysis weight, and once due to the probability of publication bias. Several single studies compared two different irrigants without antibacterial properties or compared two different antiseptic agents or two different antibiotics. No studies compared antibiotics with antiseptics. The great majority of these studies were underpowered and had limited reporting of methodology. Only one comparison was represented by more than one study (icodextrin versus lactated Ringer's solution) and this was also the only comparison of this nature with adequately powered and well‐reported studies; however SSI was not the primary outcome of either study and in one study we were not clear that ambiguous data actually represented this outcome. As a consequence of the poor reporting and small numbers of participants, events or both, all of the comparisons between agents of the same class represented low‐certainty evidence. Only one comparison found that there may be a difference between the groups: there may be more SSI in participants treated with povidone iodine compared with superoxidised water (downgraded for risk of bias as well as imprecision); in all other cases, based on available evidence, there is no clear difference between the treatment groups. Individual studies represented particular classes of surgical contamination and the applicability of the evidence from the comparisons to participants in other surgical classes may be reduced by indirectness. There was low‐certainty evidence from two studies that, on average, there may be fewer SSIs in participants treated with pulsatile compared with standard (non‐pulsed ‐ pouring method) irrigation. This was based on participants undergoing clean or clean‐contaminated surgery and may therefore be only indirectly relevant to participants undergoing more contaminated surgeries. We downgraded this evidence twice for risk of bias across multiple domains in the study with the greatest weight in the analysis. Only a minority of studies reported wound dehiscence across all comparisons. For no comparison where this was reported is there a clear difference between the groups. This was low‐ or very low‐certainty evidence in each case. Imprecision was a factor in all comparisons, inconsistency or high risk of bias were also present in some cases. Many studies did not report any of the secondary outcomes we specified for this review. Those that did often only reported one or two and these were most often length of hospital stay or adverse event data. We pooled data that reported mean lengths of stay and provided narrative summaries where medians were reported. With adverse event data we pooled studies that reported the number of participants in each group with an event. We documented reports of specific types of adverse events but did not analyse these with the exception of abscess formation, which we had prespecified as being of particular interest to the review; we analysed this separately. Mortality was reported in only a minority of studies; in many instances this is likely to be a consequence of there being zero events in low‐risk participants undergoing clean or clean‐contaminated procedures. Outcomes related to antibiotic resistance – proportion of participants on systemic antibiotics in the 30‐day postoperative period and incidence of antibiotic‐resistant infection were especially poorly reported. There were few data and the data that were reported were often incomplete. The evidence for the impact of interventions on length of hospital stay was low or moderate certainty; where differences were seen they were too small to be clinically important. A wide range of types of surgery is included in this review and all four categories of surgery (clean, clean‐contaminated, contaminated and dirty) were represented. However, as might be anticipated, only small numbers of participants undergoing clean operations were identified. Therefore, although we did not identify a material difference between subgroups in our planned analyses based on surgical category, it should be emphasised that most of the data relate to clean‐contaminated, contaminated or dirty surgeries. Only one very small study assessed the comparison of no intervention with intervention in participants undergoing clean surgery and numbers were low for the comparison between antibacterial and other solutions too. A substantial number of studies included only women because of the nature of the surgery undertaken (e.g. caesarean sections), although we do not believe this would impact on the relevance of the results to all surgical patients. Few studies included only children although many included both adults and children. Publication dates of included studies ranged from 1968 to 2016. This is likely to be a source of considerable differences between participants and surgical techniques, while the development of antibiotic resistance over time may also make results from early studies less directly relevant to current practice. Twenty of the 59 studies ‐ approximately one third ‐ were published before 1990. There were variations in the use of prophylactic antibiotics, as would be anticipated given the different types and contamination levels of surgery involved and the time span across which studies were conducted and published. This may affect the applicability of some of the evidence. We did not include studies that compared irrigation with another intervention, so can present no evidence for the value of irrigation compared with, for example, antibiotics delivered by another method. This represents a gap in the comprehensive evidence synthesis but other reviews have included these studies (see Agreements and disagreements with other studies or reviews ). We would have included any studies that compared the use of an antibiotic solution with an antiseptic solution but none were identified. This is a clear gap in the evidence and possible methods for dealing with this are discussed in Implications for research . We also did not identify any studies that compared the use of different volumes of the same solution. Although the great majority of included studies reported the primary outcome of SSI, few reported wound dehiscence and participant numbers were such that there was insufficient power for a difference between groups to be detected. Key secondary outcomes such as adverse events and antibiotic resistance were poorly and inconsistently assessed and reported in most trials and for most comparisons. Mortality was reported in only a minority of studies, although we believe that this is at least partially explained by a zero incidence in many studies not being formally reported. Although we planned to look at the time points of outcome assessment, in practice the overwhelming majority of data related to short‐term post‐surgical assessment at between two and eight weeks. Long‐term follow‐up was rare and limited to a small number of orthopaedic or spinal operations, which followed participants for several months, but even in these cases they reported limited data beyond the initial postoperative period. This is unlikely to be a serious threat to the applicability of the results for SSI but it may have implications for other outcomes such as mortality. Despite searching multiple databases and extensive citation checking we are not confident that we have identified all extant studies although we believe we are likely to have identified the great majority of published studies. Analysis of funnel plots for comparisons of intervention versus no intervention and for antibacterial versus non‐antibacterial interventions suggested that publication bias was possible or likely. The implications of this are explored in Potential biases in the review process . In studies that compare irrigation with no irrigation or compare different irrigation techniques it is difficult or impossible for personnel to be blinded to treatment allocation. Since none of these studies explicitly reported doing so, we classified them all as being at high risk of performance bias. However we did not downgrade for this risk of performance bias if no other domain was classed as posing a high risk of bias. Blinding of outcome assessment is a more important risk of bias and this was reported to be low for only a minority of studies; in many more it was unclear whether this was undertaken for the key outcomes of SSI and wound dehiscence. Just under half of studies were at risk of bias other than inherent performance bias, and the great majority were poorly reported in multiple domains, placing them at unclear risk of bias on many factors. Where possible we conducted preplanned sensitivity analyses, which looked at the impact of removing studies at a high risk of bias in one or more domains; we were able to do this for the outcome of SSI for the comparisons between irrigation and no irrigation and between antibacterial and non‐antibacterial irrigation. When we performed the sensitivity analysis for the comparison of no irrigation with irrigation we did not remove studies which were only at high risk in the domain of performance bias, because all studies necessarily had a high risk in this domain. The results of these sensitivity analyses suggested that data from studies with a high risk of bias were not acting to increase an estimate of effect, although such studies included large numbers of participants. Poor reporting means that we are not confident that most of the studies that did not show a clear high risk of bias in any domain are free from such a risk; it is likely that many are but that this is not evident from the limited reporting of the study. Finally as noted in Overall completeness and applicability of evidence and Potential biases in the review process , we are concerned that the certainty of the evidence may be compromised by selective incompleteness ‐ a pattern of missingness which may serve to increase the estimates of effect. We believe that this review is unlikely to be affected by language bias; it includes studies in Slovak, Korean, Persian, French and Danish. Studies in other languages, including Chinese and German were also identified and considered for inclusion at full text (see Excluded studies ). We identified a substantial number of trials through citation searching in addition to those found through database and trial registry searches. However, while we have some confidence that we are likely to have identified the great majority of relevant published studies, we cannot rule out the possibility that there are unpublished studies which are not included in the review and which may have affected the results. We were able to construct funnel plots for the primary outcome of SSI for both the comparison of irrigation with no treatment and the comparison of antibacterial with non‐antibacterial solutions. In the latter case there was a strong suggestion that there may be small studies with negative results that were absent from the evidence identified and we downgraded the certainty of the evidence once because of this. The appearance of the funnel plot for the comparison with no treatment was ambiguous, while we could not rule this out there was no clear suggestion of a publication bias effect. There were too few trials in the other analyses to permit funnel plot analyses so we are unable to assess the likelihood of publication bias in these sections of the review; it is nevertheless possible that it may be present. The impact of publication bias of the type we may have identified is to increase the estimate of effect relative to the true effect of the intervention. The exploratory subgroup analysis, which we used to confirm our strategy of comparing any type of irrigation with no irrigation, suggested that none of the heterogeneity in that analysis was explained by whether the solution used was antibiotic, antiseptic or antibacterial. However, we have identified that there may be fewer SSIs in participants treated with antibacterial (antiseptic or antibiotic) irrigation compared with no irrigation. The fact that we found no evidence of a differential effect of solution type in the comparison with no irrigation may represent an additional reason for caution in the interpretation of this data, alongside the noted risks of bias and publication bias. Equally, however, it is important not to over interpret subgroup analyses, particularly when these are not prespecified. We should also note that the two analyses (irrigation versus no irrigation; antibacterial versus non‐antibacterial) contained different proportions of participants in the different surgical categories, meaning that baseline incidence of SSI will differ. In the majority of the included studies the source of funding was not reported and where it was reported it was mostly non‐commercial. Whilst it is possible that funding may play a role in the potential differential absence of small negative trials, it may be more likely due to the other factors including the reluctance of both journals and authors to pursue publication in such cases. We identified only one completed study that was without extant publication in our search or trial registers, this had only recently passed its completion date; we also identified one study that had passed the planned completion date but that did not have an identified publication. We identified a number of reviews as being relevant to this synthesis; these proved extremely helpful to our citation searching although none had the same scope as our review in all respects. Existing reviews fell into the following classes: reviews focusing on a particular type of surgery (e.g. Mueller 2015 ); and reviews focusing on a particular agent or class of agents (e.g. Fournel 2010 and Oliveira 2008 , which look at the use of intraoperative povidone iodine); in some cases they focused even more narrowly on a specific intervention for a specific operation (e.g. Eke 2016 ; Smaill 2014 ). Some reviews differed from our work in that they included studies other than RCTs ‐ either quasi‐RCTs (some of which were classed as RCTs) or even less rigorous research methodologies. Some also used a very wide definition of irrigation or had a broader objective and included any method of topical application of their agent of interest to the wound, including, for example, assessments of aerosols, dry powder or very low volumes of liquid. There were also broader definitions of the area irrigated; we did not include studies where only internal (e.g.) uterine, bladder or bowel irrigation was reported. We have employed a narrower definition of irrigation but adopted a much broader approach to the types of agents and classes of surgery which were of interest. Several reviews also considered comparisons that were outside the scope of our review because the use of irrigation of a particular type was not the only systematic difference between the treatment groups. Finally our review has a much more recent search than many of these and, while many studies in the review were old, over a third of the included studies ‐ including many of those with large numbers of participants and stronger methodologies ‐ were published from 2010 onwards, with a significant number having 2015 and 2016 publication dates. The most recent review, and the one with the closest scope to ours is De Jonge 2017 , which focuses on prophylactic irrigation; this review supported the recent recommendations of the World Health Organization on prevention of SSI ( WHO 2016 ). For a number of reasons De Jonge 2017 included fewer studies than our review as it excluded studies where wounds could already be considered to be infected (and where treatment was therefore not considered prophylactic) and was restricted to irrigation at the level of the wound rather than deeper (e.g. peritoneal) irrigation. The authors also required that there be a description of appropriate antibiotic prophylaxis, which we did not; many of the studies included here had very limited reporting of co‐interventions and reporting of antibiotic use varied. There were other variations in the inclusion criteria ‐ including a restriction by De Jonge to four, widely spoken European languages whereas we applied no language restrictions. A combination of these factors accounts for many of the differences between their review and ours. One principal result of the differing inclusion criteria is that our review includes many studies in obstetric surgery, which are not included in theirs. A small number of trials, which were included in their review, were excluded from ours based on differing interpretation of adequate randomisation or volume of liquid required for irrigation.

To assess the effects of wound irrigation and intracavity lavage on the prevention of surgical site infection (SSI).