Types of studies

We included randomised controlled trials (RCTs) and cluster RCTs comparing one skin antiseptic regimen (a single agent or a combination of agents) with another regimen (a single agent or a combination of agents, placebo or no antisepsis). We excluded cross‐over studies due to the possible contaminating effect of one intervention over another. We also excluded studies assessing CVCs for haemodialysis, as this is covered by another Cochrane review (McCann 2010).

Types of participants

We included studies involving adults and children cared for in a hospital setting (in adult or paediatric wards or ICUs) with any underlying illness and a CVC inserted for any reason during the study period. Studies that enrolled a patient more than once were acceptable provided that the enrolment took place in separate hospital admissions. We excluded studies conducted in neonatal settings, for example in a neonatal intensive care unit (NICU), as the types of catheters used, the insertion site and techniques, the possible complications as well as the risk factors for sepsis are different compared with those in older children and adults (Trieschmann 2007).

Types of interventions

Types of outcome measures

Electronic searches

We searched the following databases for relevant RCTs:

• The Cochrane Wounds Specialised Register (searched 23 May 2016);

• The Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library) (2016, Issue 4);

• Ovid MEDLINE (including In‐Process & Other Non‐Indexed Citations and Epub Ahead of Print) (1946 to 23 May 2016);

• Ovid EMBASE (1974 to 23 May 2016);

• EBSCO CINAHL Plus (1937 to 23 May 2016).

We used the search strategy in Appendix 3 to search the Cochrane Central Register of Controlled Trials (CENTRAL). We adapted this strategy for Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL Plus which can be found in Appendix 4, Appendix 5 and Appendix 6, respectively. We combined the MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity‐ and precision‐maximising version (2011 revision) (Lefebvre 2011). We combined the EMBASE search with the Ovid EMBASE filter developed by the UK Cochrane Centre (Lefebvre 2011). We combined the CINAHL searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2015).

We searched the following trial registries for details of ongoing clinical trials and unpublished studies.

• ClinicalTrials.gov (http://www.clinicaltrials.gov/).

• WHO International Clinical Trials Registry Platform (http://apps.who.int/trialsearch/Default.aspx).

• EU Clinical Trials Register (https://www.clinicaltrialsregister.eu/).

Searching other resources

We checked for further reports of eligible studies using the citation lists of papers identified by the above strategies. We also scanned references lists of relevant Cochrane reviews and guidelines and contacted experts in the field.

Selection of studies

Two review authors (NML, EOR) independently assessed the first round of search results for potentially relevant studies. We retrieved in full those that appeared to meet the inclusion criteria, or where this could not be determined, for further assessment. Two review authors independently assessed the full papers retrieved, resolving any disagreement with input from a third review author (NC). We included the studies if they fulfilled the criteria for inclusion as outlined above and if the amount of information contained in the article enabled the extraction of outcome data for meta‐analysis.

We screened publications for duplicate reports of the same trial and contacted the trial authors for clarification when necessary. If we confirmed a duplicate publication, we identified a primary reference, but extracted unique data from all versions.

Data extraction and management

Two pairs of review authors (NAL and NML, PL and EOR) independently extracted and coded all data for each included study using a pro forma designed specifically for this review. Each pair was responsible for half of the total number of included studies. We extracted the following information on each study: study design, participants, setting, sample size, nature of intervention, comparison, outcomes, methods (unit of allocation and analysis) and results. We screened for duplicate entries of patients, where possible, by matching the initial number of patients recruited against the total number along each step in the conduct of the study.

We found a discrepancy between the number of catheter and the number of patients in most studies. This was due to multiple catheters being inserted in some patients who were enrolled after each insertion. We were unable to limit our analysis to one catheter per participant as none of the studies provided the data in this format.

We resolved any disagreement among the review authors by discussion and formulation of a consensus acceptable to all members of the review team.

Assessment of risk of bias in included studies

Two authors (NAL and NML) independently assessed each included study using the Cochrane tool for 'Risk of bias' assessment (Higgins 2011a). This tool addresses six specific domains.

1. Sequence generation

2. Allocation concealment

3. Blinding

4. Incomplete outcome data

5. Selective outcome reporting

6. Other issues (e.g. extreme baseline imbalance, design‐specific risks of bias such as recruitment in cluster for cluster‐RCT, block randomisation of unblinded trials or fraud).

We present detailed criteria on which we based our judgement in Appendix 7. We assessed blinding and completeness of outcome data for each outcome separately. We completed a 'Risk of bias' table for each eligible study. We resolved any disagreement among the review authors by discussion to achieve a consensus. We presented an overall assessment of the risk of bias using a 'Risk of bias summary figure', which presented all of the judgement in a cross‐tabulation of study by entry. This display of internal validity indicated the weight the reader may give to the results of each study.

In addition, we assessed whether trials followed a standard protocol for all groups under study with regard to the insertion, use, maintenance and removal of CVC, and regarding the concurrent use of other antiseptic measures such as antimicrobial impregnated CVCs, antiseptic‐soaked dressing and prophylactic antibiotics. We referred to the study protocol, where available, for further details if necessary. We made relevant remarks in the corresponding 'Risk of bias' table for each study if there were significant concerns in this aspect.

Measures of treatment effect

For dichotomous data, we used risk ratio (RR) to measure outcome estimates of the same scale. We estimated the number needed to treat for an additional beneficial outcome (NNTB) from the pooled risk difference (RD) using an online NNTB calculator (http://nntonline.net/visualrx/). For continuous data, we pooled measures at a similar time point using the mean difference (MD). Two studies reported the measure of variance as a standard error (SE) or 95% confidence intervals (CI) (Humar 2000; Dettenkofer 2010). We obtained standard deviations (SD) for the above‐mentioned studies from the SE using the formula SD = SE x square root of the number of participants, and from the 95% CI using the formula SD = square root of the number of participants x (upper limit or CI − lower limit of CI)/3.92.

Unit of analysis issues

One potential unit of analysis issue that we had anticipated was the issue that arose as a result of the studies using catheters, rather than patients, as the unit of analysis in catheter‐related outcomes such as catheter‐related BSI and catheter colonisation. Ideally, if the study performed randomisation and analysis based on the participants, and each participant had only one catheter evaluated, adjustment for clustering would not have been necessary. However, if a study included multiple catheters per patient and clearly stated so, we would have assessed whether the authors had undertaken statistical adjustment to account for the effects of clustering by using appropriate analysis models such as the 'generalised estimating equation' (GEE) model (Higgins 2011b). If investigators had made adjustments for clustering, we would have combined the study with other studies in the meta‐analysis. If they had not, or if it was unclear whether there were adjustments made, we would have assessed the number of catheters as well as participants in the study. If the studies had also reported the number of participants with events and the total number analysed, we would have only reported the outcomes using the participants, rather than catheters as the unit of analysis. However, if the study did not provide participant‐level data, we would not have been able to avoid the unit of analysis issues. We would have acknowledged this as a major limitation of the review in our discussion and undertaken sensitivity analysis to assess the pooled results after excluding studies with no adjustments for clustering.

However, in this review, none of the included studies provided participant‐level data for catheter‐specific outcomes. As a result, we could not adjust for the unit of analysis issue, nor could we perform sensitivity analysis to assess the results with and without studies with unadjusted unit of analysis issues. We have acknowledged this in our discussion, as planned.

Another possible unit of analysis issue that could have arisen was the effects of clustering that arose in cluster‐RCTs in which randomisation was performed at the unit, rather than the participant level. However, we did not include any cluster‐RCTs in this review.

Had we identified an eligible cluster‐RCT (e.g. trial in which the assignment to intervention or control group was made at the level of the unit or ward rather than the individual), we would have addressed the possible unit of analysis issues as follows.

First, we would have assessed whether the authors had made adjustments for the effects of clustering to account for non‐independence among the participants by using appropriate analysis models such as the 'generalised estimating equation' (GEE) model (Higgins 2011b).

If investigators did not make adjustments for the effects of clustering, we would have performed adjustment by multiplying the SEs of the final effect estimates by the square root of the 'design effect', represented by the formula '1 + (m − 1) x ICC', where m is the average cluster size (number of participants per cluster) and ICC is the intracluster correlation. We would have determined the average cluster size m by dividing the total number of participants by the total number of clusters. We would have used an assumed ICC of 0.10, which has been proposed to be a realistic general estimate based on previous similar studies (Campbell 2001). We would also have combined the adjusted final effect estimates from each trial with their SEs in our meta‐analysis using the generic inverse‐variance methods, as stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

If it were impossible to find out whether trialists made adjustments on the effect of clustering, we would still have included the studies concerned in our meta‐analysis using the effect estimates reported by the authors, and performed sensitivity analyses to assess how excluding those studies would affect the overall pooled estimates.

Dealing with missing data

We assessed whether there was a high attrition rate and whether an intention‐to‐treat analysis was performed. To assess whether the dropout rate was important, we inspected the absolute attrition rate and the attrition rate in relation to the event rates for the intervention and the comparison groups. If the absolute dropout rate was 20% or more, we judged the study to be at high risk of bias due to incomplete outcome data. If the dropout rate was lower than 20%, we used a 'worst‐case‐scenario' method for the primary outcomes (Guyatt 1993). For instance, for an unfavourable outcome such as catheter‐related BSI or mortality, if the results of a trial favoured the intervention group, we assumed all dropouts from the intervention group to have developed the outcome, and all dropouts from the comparison group to have not developed the outcome. We then analysed to see if such an assumption changed the direction of the results (e.g. from favouring the intervention group to favouring the comparison group). If so, we considered the dropout rate to be significant. We made the reverse assumption when a trial favoured the comparison group, or when the outcomes examined were favourable, such as survival or treatment success.

Assessment of heterogeneity

We assessed all the included studies in terms of their clinical and methodological characteristics.

1. Baseline characteristics of the participants

2. Clinical settings of the studies (e.g. intensive care units, oncology wards, renal units)

3. Co‐interventions

4. Methodological quality (as detailed in the 'Risk of bias' assessment, for example studies at high risk of bias are defined as studies with unclear or no allocation concealment, and studies where participants, caregivers or investigators are not blinded, or where blinding is unclear)

5. Nature of intervention (comparison between one skin antiseptic regimen and placebo as opposed to comparison of two active regimens)

6. Outcome assessment and unit of analysis.

We visually inspected the forest plots for any evidence of heterogeneity of treatment effects. We used the I² statistic (Higgins 2003) to measure inconsistency in the results, with a value of 50% or greater indicating moderate to substantial statistical heterogeneity.

We found significant statistical heterogeneity in one analysis (Analysis 4.4) and provided a plausible explanation the possible reason for heterogeneity in the form of risk of attrition bias in some included studies. We decided to still provide the pooled estimate for this analysis and separated the studies based on the risk of attrition bias in our pre‐specified sensitivity analysis.

Assessment of reporting biases

We planned to screen for publication bias in our review using a funnel plot if there were more than 10 studies included in the analysis. If publication bias was implied by a significant asymmetry of the funnel plot, we would have included a statement in our results with a corresponding note of caution in our discussion. We did not generate any funnel plot in this review as there were fewer than 10 studies included in the analysis across all the comparisons and outcomes.

Data synthesis

We used Review Manager software to perform meta‐analysis of the included studies (RevMan 2014). We used a fixed‐effect model for most of our analyses, as there was no substantial clinical and statistical heterogeneity. For the outcomes with substantial clinical and statistical heterogeneity that was not satisfactorily explained or reduced by subgroup analyses, we used a random‐effects model that took into account between‐study variability within the analysis and lessened the possibility of spurious inferences of significance compared to the fixed‐effect model. We used the Mantel‐Haenszel method to analyse all the dichotomous outcomes, as we anticipated relatively frequent events for most of our outcomes. For continuous outcomes, we employed the inverse variance methods using the effect measure of mean differences. In our assessment of the effects of missing data, we compared our adjusted analysis using the best‐ and worst‐case scenarios to the completer analysis as reported by the study authors.

When there were more than two arms evaluated in a study, for example, aqueous chlorhexidine versus alcoholic chlorhexidine versus aqueous povidone‐iodine, we set up separate pairwise comparisons as subgroups under the major comparison of chlorhexidine versus povidone‐iodine, as follows: aqueous chlorhexidine versus aqueous povidone‐iodine; and alcoholic chlorhexidine versus aqueous povidone‐iodine. In so doing, we halved the total number of participants and events in the povidone‐iodine group to avoid double‐counting.

Had we identified studies that assessed cost‐effectiveness, we planned to provide only a narrative review of their findings and not directly compare costs in studies using different units of measurement, due to the complexity of analysing cost‐effectiveness if different price‐years were used.

Subgroup analysis and investigation of heterogeneity

In this review, we created subgroups of comparisons based on the solution used, for example, a subgroup for chlorhexidine in aqueous solution versus povidone iodine in aqueous solution, and another subgroup for chlorhexidine in alcohol versus povidone‐iodine in aqueous solution.

Had data been available, we would have carried out the following subgroup analyses:

1. Short term CVCs (less than 10 days) versus longer term CVCs (10 days or more)

2. CVCs with antimicrobial modifications (antimicrobial impregnation, cuffs, hubs) versus CVCs with no antimicrobial modifications

3. Studies undertaken in paediatric patients versus adult patients

4. Studies undertaken in different patient populations with different levels of care (intensive care patients, oncology patients, renal patients and patients in general medical or surgical wards)

5. Studies undertaken with co‐interventions (e.g. sepsis prevention bundle) versus studies done without co‐interventions

6. Studies that used rigorous criteria (e.g. as outlined in Pagani 2008) for determining catheter‐related infections versus studies that used more liberal criteria.

Sensitivity analysis

We performed the following sensitivity analyses.

1. Best‐ and worst‐case scenarios to assess the impact of missing data, as described in the section 'Dealing with missing data'.

2. Including and excluding studies with unclear and high risks of selection bias, namely, studies with unclear or high risk for random sequence generation, allocation concealment or both.

Had sufficient data been available, we would have performed additional sensitivity analyses to include and exclude studies with methodological issues other than selection bias, such as a lack of blinding to the participants, caregivers or investigators, or where blinding was unclear.