Interventions

The use of gloves, gowns, aprons or masks by any hospital staff (healthcare or non‐healthcare professionals) or by any patient's caregiver or visitor for interactions with a patient colonised or infected with MRSA or with potentially contaminated areas in the patient’s environment, for example in the patient's room, cubicle or operating room. We considered the use of 'medical gloves'. To be eligible, gloves needed to be disposable and intended for single patient use and then to be discarded. We considered the use of 'gowns', either 'isolation gowns' or 'surgical gowns'. For 'masks', we considered the use of 'procedure masks' and 'surgical masks', as well as 'particulate respirators' (see glossary in Appendix 1 for a definition of all these terms).

We defined as eligible any 'care bundle' (see Appendix 1) that considered the use of gloves, gowns or masks, or any combination thereof. Therefore, gloves, masks and gowns could be used in the following ways:

• on their own as a single intervention, for example, the use of gowns alone;

• as a combination, for example, the use of gowns and gloves;

• combined with any other barrier precaution, such as the placement of MRSA patients in isolation units to be attended by staff using gowns, gloves and masks; or

• combined with any other infection control intervention, such as the decolonisation of patients with MRSA.

Only studies in which gloves, gowns or masks were used with patients who had MRSA were eligible. As a consequence we excluded studies that investigated the effects of the following interventions:

• gloves, gowns or masks as 'routine practice' or 'standard precautions', that is, when there is anticipated exposure to a patient’s blood, body, fluids, secretions,and excretions (except for sweat), non‐intact skin, draining wounds and mucous membranes (Siegel 2006; Johnston 2009). Therefore, we excluded studies assessing gloving, gowning or masking during routine vascular catheter insertion, surgical procedures, and patient care after organ transplantation (Stewart 2006; Tanner 2006; Lipp 2014; Mischke 2014);

• the universal use of gloves, gowns or masks, that is, their use for contacts with all patients (Webster 2003); or

• the pre‐emptive use of gloves, gowns or masks, that is, their use for all new admissions or for all patients admitted to a specific unit, until a negative screening culture for the target organism is reported (Siegel 2006).

Comparators

We considered any comparator, provided that it allowed the effects of gloving, gowning or masking (used on their own or in combination) for interactions with patients colonised or infected with MRSA or with their environment to be assessed in their own right. In practical terms, we would have included those studies in which co‐interventions were similar in the study groups, as this would allow us to assess the specific impact of the use of gloves, gowns or masks.

We excluded studies that evaluated the effects of MRSA screening programs, isolation of MRSA patients (such as placement in an isolation unit or ward, nurse cohorting or cohorting without designated staff), or campaigns to increase the use barrier precautions, as these do not allow the effects of the use of gloves, gowns or masks to be assessed in their own right. For example, in studies evaluating MRSA screening programmes the observed effects could be attributed to early detection of MRSA carriers (which implies that they do not become a continuous source of MRSA), and not only to the use of gloves, gowns or masks.

See Differences between protocol and review for this section.

Primary outcomes

Secondary outcomes

• MRSA to meticillin‐susceptible S aureus (MSSA) ratios.

• Length of stay, measured in days (see glossary in Appendix 1).

• Antibiotic use.

• All cause mortality.

We did not exclude any study solely because no outcomes of interest were reported. We did not attempt to assess issues of equity and relevance of evidence to specific populations. See Differences between protocol and review for this section.

All study designs (clustered or not) except for ITS, CITS and RMS

We would have assessed the RoB according to the domains proposed by the Cochrane Collaboration’s RoB tool and the Cochrane EPOC group (Higgins 2011a; EPOC 2013c).

• Random sequence generation (selection bias).

• Allocation concealment (selection bias). This domain also considers the presence of recruitment bias in cluster‐designs.

• Imbalance in baseline characteristics (selection bias), in terms of either the individuals or the clusters (when it is a cluster design). See Appendix 3 for the list of potential confounders to consider. This domain will not be assessed for RCTs allocated at the individual level with an adequate sample size as we will assume that baseline imbalances in these designs are caused by chance.

• Imbalance in baseline outcome measurements (selection bias), when applicable (assessments to be made for each outcome (or class of outcomes); EPOC 2013c).

• Blinding of participants and personnel (performance bias). The Cochrane Handbook for Systematic Reviews of Interventions suggests making the assessments for this domain separately for different outcomes (Higgins 2011a; Section 8.5.1), however, we would have assessed this domain for each study as a whole, as we assumed that the lack of blinding of participants or healthcare providers would distort the actual results of all the review outcomes in a similar manner.

• Blinding of outcome assessment (detection bias). We planned to group the outcomes by the susceptibility of their measurement to the lack of blinding (with assessments to be made for each outcome (or class of outcomes), as follows:

  • high susceptibility: healthcare‐associated MRSA colonisations; healthcare‐associated MRSA infections; healthcare‐associated MRSA bacteraemias; healthcare‐associated MRSA pneumonias; mortality attributable to MRSA; prevalence of carriers of MRSA.

  • low susceptibility: MRSA to MSSA ratios; length of stay; antibiotic use; all cause mortality.

• Incomplete outcome data (attrition bias; with assessments to be made for each outcome (or class of outcomes); loss of clusters in cluster‐designs will be also assessed).

• Selective reporting (reporting bias).

• Protection against contamination (EPOC 2013c).

• Timing of the assessments of the outcomes (with assessments to be made for each outcome (or class of outcomes).

• Statistical methods taking the clustering into account (only for cluster designs; Higgins 2011b).

See Appendix 4 for details of criteria on which the judgements would have been based. This tool contains also the domains that would have been considered when assessing the RoB of cluster designs.

The following were defined as 'key domains' for the analysis: random sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, and incomplete outcome data.

ITS, CITS and RMS

We would have considered the tool proposed by the Cochrane EPOC group (EPOC 2013c), which has the following domains.

• Was the intervention independent of other changes?

• Was the shape of the intervention effect pre‐specified?

• Was the intervention unlikely to affect data collection? (Assessments made for each outcome (or class of outcomes)).

• Blinding of outcome assessment (detection bias; assessments made for each outcome (or class of outcomes)).

• Incomplete outcome data (attrition bias; assessments made for each outcome (or class of outcomes)).

• Was the study free of selective outcome reporting (reporting bias)?

See Appendix 5 for details of criteria on which the judgements would have been based. All the domains except for 'selective reporting' were defined as 'key domains' for the analysis.

As this systematic review focuses on non‐pharmacological interventions, we would have assessed the blinding of participants and personnel and the blinding of outcome assessors following the suggestions of the 'CLEAR NPT checklist' (Boutron 2005). We also planned to assess the quality of reporting of the blinding of patients, 'care providers', 'persons caring for participants' and 'data analyst' as this checklist proposes, but these items would not have been considered for the global rating of the RoB of the study.

We planned to assess most of the domains for each study as a whole (therefore, by a single entry in the RoB tool for each study). However, some domains would have been assessed separately for each individual outcome (and for each time point for the same outcome if several time points are considered). Therefore, we would have assigned a single entry in the RoB tool for each outcome‐time point. On the other hand, we planned to limit the number of entries used by grouping outcomes within every study, the same grouping would have been applied to every study in the review. Appendix 6 details how we planned to group the outcomes for the RoB assessment.

At least two review authors would have independently assessed the RoB of each included study (not masked to the study details). Each domain of the RoB tool would have been labelled as 'low RoB' (plausible bias unlikely to seriously alter the results), 'high RoB' (plausible bias that seriously weakens confidence in the results); or 'unclear RoB' (plausible bias that raises some doubt about the results). We planned to obtain the information from the reports but, if there had been not enough information we would have contacted the authors or the organisations for clarification. If clarification had not been obtained, we would have assigned a grading based on the available information and the consensus between the review authors. Disagreements would have been resolved by discussion and consensus, and by consulting a third review author if necessary. We planned to assess inter‐rater reliability for the key domains by using the kappa statistic (Higgins 2003), and we planned to report relevant discrepancies in the assessments.

We would have justified judgements of RoB and provided this information in a ‘Risk of bias table’ for each included study; we would have reported the source of information for each RoB judgement, including those based on assumptions made on information provided outside publicly available documents. We would have reported the results of assessments of confounders in an additional table, listing the pre‐stated confounders as columns and the studies as rows (Reeves 2011; see Appendix 3 for the list of potential confounders). Two figures would have been also included: a ‘Risk of bias graph’, presenting an overview of our judgements across each RoB domain, and a ‘Risk of bias summary’, to show an overview of judgements for each RoB domain for each study.

We planned to summarize the RoB for each outcome (or class of similar outcomes) in two different manners, 'within each study' and 'across studies' (Higgins 2011a):

We would have provided a narrative summary of the RoB among the included studies. Summary assessments of RoB for each outcome across studies would have been incorporated into explicit measures of the quality of evidence for each important outcome using the GRADE system (Guyatt 2008). See Differences between protocol and review for this section.

All study designs except for ITS, CITS and RMS

We planned to present the following estimates of the effect with their associated 95% CI.

• Risk ratio (RR): for dichotomous data, such as prevalence of carriers of MRSA.

• Odds ratio (OR): for counts of rare events and rates, such as incidence density rate of HAIs.

• Mean difference (MD): for continuous data, such as length of stay (or standardised mean difference (SMD) if the continuous data require standardisation across studies).

ITS, CITS and RMS

We planned to present, if possible, the results for each outcome as changes along two dimensions (EPOC 2013d).

• Change in level: reflecting the immediate effect of the intervention, measured as the difference between the fitted value for the first post intervention data point (one month after the intervention) minus the predicted outcome one month after the intervention based on the pre‐intervention slope only.

• Change in slope: reflecting the long‐term effect of the intervention, this is the change in the trend from pre‐ to post‐intervention.

The preferred analysis method for ITS and RMS is either a regression analysis with time trends before and after the intervention, which adjusted for autocorrelation and any periodic changes, or auto regressive integrated moving average (ARIMA) analysis (EPOC 2013d). We planned not to include, and therefore, not re‐analyse, ITS studies or RMS that had an inappropriate analysis of results.

Adjustment of the estimates of the effects

This review considered randomised and non‐randomised studies as eligible. Susceptibility to selection bias (understood as mean differences in the baseline characteristics of individuals in different intervention groups) is widely regarded as the principal difference between randomised and non‐randomised studies. NRS are more prone to confounding (that is, selection bias that gives rise to imbalances between intervention and control groups on prognostic factors because the distributions of the factors differ between groups, and the factors are associated with outcome(s); Reeves 2011).

Randomisation with adequate allocation concealment reduces the possibility of selection bias, so that differences in characteristics between groups can be attributed to chance (Reeves 2011). Therefore, for studies described by the study authors as 'randomised' we would have used unadjusted effect estimates, that is, crude estimates that have not been corrected for the effects of confounding factors. We planned to assess the effects of this decision through Sensitivity analysis (see Differences between protocol and review).

As a result of the need to control for confounding as best as possible in NRS, we would have preferred to use adjusted estimates from these studies, that is, estimates that have been corrected for the effects of confounding factors. If the study report did not provide the adjusted effect estimate, we would have attempted to obtain it by following the guidance provided by the Cochrane EPOC Group (EPOC 2013d). If the study report presented alternative adjusted estimates for the same outcome, by preference we would have used the estimate that was identified as the primary adjusted model (Reeves 2011). We would have assessed the effects of this decision through Sensitivity analysis.

Summary effect measures derived from the meta‐analyses

For each comparison and outcome, a meta‐analysis would have generated a summary effect estimate with its corresponding 95% CI. The results of each meta‐analysis would have been re‐expressed to easily interpretable statistics in the standard Cochrane 'Summary of findings' table, generated with the GRADEprofiler software (GRADEpro 2014).

• Dichotomous outcomes and counts of rare events and rates: we planned to provide both a relative measure (e.g. RR or OR) and measures of absolute risk, all of them with their corresponding CI 95%. By preference, we would have expressed the relative measure as RR, because the OR is the hardest summary statistic to understand and to apply in practice, and many practising clinicians have reported difficulties in using it (Deeks 2011); therefore, if the meta‐analysis were based on ORs its global estimate would have been an OR, but we would have re‐expressed it as RR by applying the formula described in section 12.5.4 of the Cochrane Handbook for Sytematic Reviews of Interventions (Schünemann 2011). In addition, we planned to re‐express the relative measure using absolute effect measures (risk differences). We would have calculated RRs and risk differences from a plausible range of control group event rates from the individual trials.

• Continuous data: we planned to provide an absolute measure alone, the MD or SMD, and its 95% CI.

See Differences between protocol and review fro this section.

Studies with allocation to interventions at the group level

We expected that many eligible studies would be cluster designs (studies in which the unit of allocation is not a person, but instead is a group of people). If these designs were included, we would have determined whether the data were correctly analysed: comparisons that allocate clusters (for example, groups of professionals or wards) but do not account for clustering during analysis have potential 'unit of analysis errors’, resulting in artificially extreme P values (see Appendix 1) and over‐narrow confidence intervals (Ukoumunne 1999). For cluster designs, we would have considered data as analysed correctly if:

• the analysis was conducted at the same level as the allocation (i.e. at the 'cluster’ level);

• the analysis was conducted at the level of the individual, but appropriate statistical correction for the clustering was performed (such as generalised estimating equations (GEE), mixed models, or multilevel models); or

• the analysis was conducted at the level of the individual, but the sample size was reduced to its ‘effective sample size’, or the variance was inflated by the design effect.

If the data analysis had been performed incorrectly we would have attempted to perform an 'approximately correct analysis' following the guidance of Section 16.3 of the Cochrane Handbook for Sytematic Reviews of Interventions (Higgins 2011b). We planned to contact the authors to obtain relevant data, when necessary. If, finally, these data were not available, the results of the study would have been reported as point estimates of the intervention effect without presentation of any statistical analysis (P values) or confidence intervals and they would have not been included in the meta‐analysis (Higgins 2011b).

Sample size calculation

We planned to assess whether the unit of allocation had been taken into consideration in the sample size calculation or power calculation. In cluster designs the sample size estimate has to be inflated to take account of the cluster design (Ukoumunne 1999), so we planned to evaluate whether the sample size had been estimated based on the intra‐cluster correlation co‐efficient (see Appendix 1), however, this would have not been considered for the assessment of the RoB.

Outcome is an event that may re‐occur

If the outcome of interest would have been an event that may re‐occur (such as HAIs), we would have assessed whether the count data had been treated erroneously, that is, as if they were dichotomous data (Deeks 2011).

Additional analysis issues

We planned to examine critically the statistical approaches of the included studies.

• We would have assessed whether the statistical approach relating to infection or colonisation outcomes was adequate. For communicable diseases, unless outcomes are independent, the risk to one patient will depend on the status of other patients. For this reason, the use of approaches that assume independence (which include the Chi² test, Fisher’s exact test, linear regression, etc.) can lead to false inferences, and statistical approaches able to account for dependencies in the outcome data should be used instead (Stone 2007). We did not plan to consider our conclusion regarding the statistical approach as part of the global rating of the RoB of the studies.

• For ITS and RMS designs we would also have assessed whether the statistical approach had ignored secular (trend) changes. Analysis of aggregated data of the pre and post intervention phases should be avoided because it does not provide information about trends over time. We had planned to exclude ITS and RMS that did not have a parallel control group that ignored secular changes, and had performed a simple test of the pre versus post intervention periods, from the review without further justification (these studies will be considered as uncontrolled before‐and‐after studies).

See Differences between protocol and review for this section.

Missing outcome data

As far as possible, we planned to apply an 'intention‐to‐treat' analysis for all outcomes, that is, an analysis that fulfils the following principles (Higgins 2011b).

• Participants are kept in the intervention groups to which they were randomised, regardless of the intervention they actually received.

• There is a measurement of outcome data for all participants.

• All randomised participants are included in the analysis.

We planned to contact the primary authors for missing data and clarification of issues. If we could not obtain this information, we would have documented this on the data extraction form and within the text of the review, and we would have performed an ‘available case analysis’, that is, an analysis that includes data on only those participants whose results are known, and that uses as denominator the total number of people who had data recorded for the particular outcome in question. In the available case analysis the participants would have been analysed according to the group to which they were randomised. If possible, we would have ‘re‐included’ avoidable exclusions done by the authors (Higgins 2011b). We planned to perform Sensitivity analysis to assess how sensitive results were to changes in the assumptions made in the available case analysis.

We would have described missing outcomes for the included studies by reporting proportions of allocated participants for whom no outcome data were obtained (with reasons) by outcome and by study group. We planned to explore the impact of the missing outcome data in the overall treatment effect through Sensitivity analysis by excluding studies with high RoB for the domain 'Incomplete outcome data' from the meta‐analysis. We would have described in the Discussion the impact of the missing outcome data on the findings of the review.

Other missing data

If other relevant data were not directly reported (for example, standard deviation for continuous data), we would have obtained this information by looking carefully in the report for statistics that would allow its calculation. If this was not possible, we would have tried to contact the primary authors. If, finally, we could not obtain the information, we would have recorded this in the data extraction template and we would have imputed this information following the suggestions provided in Higgins 2011c.

See Differences between protocol and review for this section.

Quality of the body of the evidence

We would have assessed the quality of the body of the evidence according to the GRADE approach (Schünemann 2011). We would have presented at least one standard 'Summary of findings' table developed using GRADEprofiler (GRADEpro 2014). A ‘Summary of findings’ table provides key information concerning the quality of evidence, the magnitude of effect of the interventions examined, and the sum of available data on all important outcomes for a given comparison.

See Differences between protocol and review for this section.