Decontamination of environmental surfaces in hospitals to reduce hospital acquired infections

Notes

Editorial note

This protocol will not be progressed to review stage.

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To assess the effects of decontaminating hospital environmental surfaces (based on cleaning, disinfection or sterilization) on hospital acquired infections in patients and staff.

Background

Description of the condition

Healthcare‐associated infections (HCAIs) can occur in any care setting however the majority involve hospitalised patients, who tend to have more risk factors and higher rates of infection than outpatients (Siegel 2006; Ranji 2007). 

HCAIs are caused by a variety of microorganisms, mostly bacterial (e.g. Staphylococcus) and viruses (e.g. Norovirus). However, the presence of a microorganism in the hospital setting is not the only determinant for developing infection (Dettenkofer 2001). Risk factors for hospital‐acquired infections include:

• Patient susceptibility, such as advanced age, severe underlying diseases or decreased immunity (Ward 1981).

• Invasive interventions, such as surgery, biopsies, or intubation (WHO 2002; Siegel 2006).

• Prolonged antimicrobial therapy (Peacock 1980; Boyce 1981).

• Environmental factors, such as the concentration of patients highly susceptible to infection in intensive care units, also contribute to the transmission of pathogens (Dettenkofer 2001). Moreover, the physical environment in hospitals provides a reservoir for organisms that could potentially cause infection. Microorganisms can be found on hospital surfaces, objects and medical devices that finally contact susceptible body sites of patients, directly or indirectly via healthcare professionals (WHO 2002).

Hospital‐acquired infections (i.e. healthcare‐associated infections acquired by hospitalised patients) occur worldwide and affect both developed and resource‐poor countries. According to the Centers for Disease Control and Prevention (CDC), in the USA alone hospital‐acquired infections cause about 1.7 million infections (or infections in approximately 5% of hospital patients) per year (Klevens 2007; Curtis 2008; Ranji 2007). Higher rates of incidence are reported in developing countries (WHO 2002). Moreover, the incidence of hospital‐acquired infections appears to have increased over the last three decades (Weinstein 1998), despite the fact that most are thought to be preventable (Harbarth 2003).

A proportion of hospital‐acquired infections are attributed to drug‐resistant organisms, such as methicillin‐resistant Staphylococcus aureus (MRSA), vancomycin‐resistant Enterococci (VRE) or Acinetobacter spp. and other multi‐resistant Gram‐negative bacilli (e.g. E.coli, Klebsiella spp.). In most instances, there are limited options for treating these infections (Siegel 2006). For the purposes of this review we will consider the

Description of the intervention

Various strategies exist for controlling healthcare associated pathogens in the hospital setting: early detection (laboratory surveillance and screening for MRSA); infection control measures (hand washing, gloving, gowning, masking, isolation of colonised and infected patients, decolonisation therapy, cleaning of hospital environmental surfaces); and rational antibiotic use (Loeb 2003). Most institutions use a combination of these strategies.

This review will focus on the impact of cleaning environmental surfaces in controlling hospital‐acquired infections, considered as a routine activity or as an infection control intervention implemented when infection rates are noted to be increasing or exceeding a recognised benchmark (for example, during outbreaks).

All forms of cleaning will be considered, such as cleaning with detergents alone or cleaning followed by disinfection, irrespective of the type of products used or the techniques applied.

How the intervention might work

Many healthcare‐associated pathogens are easily transferred from patient‐to‐patient, either via the hands of health care workers (Handwerger 1993; Chang 2000) or through the contamination of inanimate objects, including clothing or equipment (Byers 1998; Mayfield 2000).

Most of the microbial pathogens that cause hospital‐acquired infections have an innate ability to survive on surfaces in the hospital environment (Dancer 1999). MRSA, Acinetobacter and Norovirus can be recovered from a huge variety of surfaces in hospitals (Getchell‐White 1989; Wagenvoort 2000; Wu 2005). VRE may cause outbreaks that are difficult to control, partly due to their extreme longevity in the hospital environment and their resistance to routine cleaning (Dancer 1999). Environmental contamination with Clostridium difficile is accepted as a risk factor for the acquisition of this bacterium (Kaatz 1988).

As pathogens can survive on surfaces in the hospital environment, contact by health care personnel or by the patients with contaminated surfaces may result in the final transmission of pathogens to the patients, increasing the risk of hospital‐acquired infections (Rutala 2001). Surfaces that are frequently touched by hands are thought to provide the biggest risk for patients (Bhalla 2004; Dancer 2008a; Dancer 2008b).

Considering this transmission cycle for healthcare associated pathogens in the hospital setting, there is enough evidence to suggest that the decontamination of hospital surfaces may reduce hospital pathogen levels and risk of hospital‐acquired infections (Curtis 2008).

Why it is important to do this review

Hospital‐acquired infections are a significant burden both for the patient and for public health (WHO 2002), because of their frequency and their attributable morbidity, mortality, lengths of stay, and costs (Sheng 2005; Siegel 2006). Hospital‐acquired infections contribute significantly to the escalating costs of health care. The overall annual direct medical costs of hospital‐acquired infections to US hospitals ranges from $28.4 to $33.8 billion. On the other hand, it has been argued that infection control interventions are cost‐effective and the benefits of prevention range from $5.7 to $31.5 billion (Scott 2009).

Traditionally, the visual experience of dirty hospitals has been linked with the risk of hospital‐acquired infections but there may be little evidence to support this at present (Dancer 1999). There has been much debate over hospital cleanliness and increasing numbers of hospital‐acquired infections. However, a number of studies suggest that cleaning or disinfection of the environment can reduce transmission of healthcare‐associated pathogens (Boyce 2007).

Infection control teams do not usually question the importance of thorough environmental cleaning for controlling outbreaks of healthcare associated pathogens. However, its importance as a stand‐alone activity remains controversial (Dancer 2009) and little is known about the best way to clean in non‐outbreak settings (Tankovic 1994; Scerpella 1995; Denton 2004).

Finally, whether hospital cleaning staff should use disinfectants or detergents for routine cleaning continues to be controversial and the practice varies widely (Mayfield 2000; Verity 2001; Wilcox 2003). Although disinfectants may be effective in preventing hospital‐acquired infections, they also may lead to the development of resistances among nosocomial pathogens and allergies among patients and staff. On the other hand, the additional costs and the environmental pollution associated with the use of disinfectants should be borne in mind (Rutala 2001; Dettenkofer 2007; Exner 2007). 

Objectives

To assess the effects of decontaminating hospital environmental surfaces (based on cleaning, disinfection or sterilization) on hospital acquired infections in patients and staff.

Methods

Criteria for considering studies for this review

Types of studies

The randomised controlled clinical trial (RCT) is generally considered to have the highest level of internal validity (by eliminating selection bias) with regard to assessing the efficacy of an intervention. However, individual level randomisation is often difficult to achieve in the context of infection control interventions due to ethical concerns, logistical difficulties (by definition an environmental infection control intervention impacts on multiple people) or a need to intervene quickly (Harris 2004). For these reasons, non‐randomised designs, whilst more prone to bias, are ubiquitous in the infectious diseases literature, particularly in the area of interventions for decreasing the spread of antibiotic‐resistant pathogens (Harris 2004). 

There is no standardised nomenclature for non‐randomised designs. This may cause problems when defining the types of studies to include in a systematic review and when deciding on the eligibility of the primary studies. For this reason, we will consider explicit study design features (not only the study design labels) for defining the types of studies to include and when deciding on the eligibility. We will consider the check‐lists developed by the Cochrane Non‐randomised methods (NRMG) group, although experience of using them is limited (Reeves 2009). If the specification of a study design label is needed, we will use the terms presented by these check‐lists.

This review will include the following study designs:  

• Randomised controlled trials (RCTs) with allocation to interventions at the individual or at the group level.

The participants (or groups of participants in cluster RCT) are assigned prospectively to an intervention or to a control group (or more than one control group) using a process of random allocation (for example, random number generation or coin flips) which theoretically ensures that the intervention and the control group differ only in the exposure to the treatment.

• Quasi‐randomised controlled trials (Q‐RCT) with allocation to interventions at the individual or at the group level.

The participants (or groups of participants) are assigned prospectively to an intervention or to a control group (or more) using a process that attempts but does not achieve true randomisation (for example, alternation of allocation, birth dates or week days).

• Controlled before and after studies (CBAs).

Participants are allocated at the individual level to groups; those in the intervention group receive an intervention and those in the control group do not. The effect of the intervention is tested by comparison of the outcomes of participants within the same group of participants before and after the intervention is introduced, and then, by comparing outcomes for participants in the control and intervention groups.

• Controlled cohort before‐and‐after studies (CChBA).

Type of non‐randomised study with allocation to the study arms at the cluster level. The clusters allocated to the intervention group receive an intervention and those allocated to the control group do not. The effect of the intervention is tested by assessment of outcomes within the same group over time both before and after the intervention is introduced, and then, by comparing the control and intervention groups. Note that 'cluster' refers to an entity (e.g. an organization), not necessarily to a group of participants, and 'group' refers to one or more clusters (Reeves 2009). The term 'cohort' designates here the new sample of individuals that is drawn from each of the clusters at each measurement occasion (Shadish 2002).

• Interrupted time series (ITS) with or without a parallel control group.

Type of non‐randomised study where trends in an outcome are measured repeatedly over multiple time points, both before and after the intervention is introduced. The intervention being examined occurs at a defined point in time so it is possible to compare the outcome of interest before and after the intervention (as opposed to being compared to an external control group). Interrupted time series analysis requires knowing the specific point in the series when the intervention occurred (NHMRC 2008).

To be included in the review, CBAs and CChBAs must meet the following key criteria (EPOC 2009a):

1. contemporaneous data collection: data collection should be contemporaneous in study and control sites during the pre‐ and post‐ intervention periods of the study, using identical methods of measurement;

2. appropriate choice of control site: study and control sites should be comparable with respect to setting of care;

3. the study should include at least two intervention sites and two control sites;

4. in addition to the EPOC criteria, for CBA or CChBA studies to be eligible for this review the allocation to intervention and the assessment of outcomes must be done prospectively (looking forward and typically using data collected for the purpose of the study).  

ITS studies must meet the following criteria (EPOC 2009a):

1. clearly defined point in time when the intervention occurred (reported by the researchers);

2. the study should include at least three data points before and three after the intervention;

3. in addition to the EPOC criteria, for ITS studies to be eligible in the review, both the assessment of outcomes in the pre‐ and post‐intervention phases, and the administration of the intervention must be planned prospectively by the researchers.

We will exclude ITS studies without a parallel control group that have ignored secular (trend) changes and performed a simple t‐test of the pre versus post intervention periods.

The stepped‐wedge randomised trial design (see Table 1), a design increasingly used to assess the effectiveness of patient safety interventions (Brown 2008), will be also eligible for this review; this is a particularly relevant study design where it is predicted that the intervention will do more good than harm and/or where, for logistical, practical or financial reasons, it is impossible to deliver the intervention simultaneously to all participants (Brown 2006).

1. Glossary.

Ambulatory care facilities	Facilities which administer health services to individuals who do not require hospitalisation or institutionalisation (MESH Browser 2009).
Bloodstream infection (BSI)	Presence of live pathogens in the blood, causing an infection (see Horan 2008 for a more specific definition of bloodstream infection).
Cleaning	Removal, usually with detergent and water or enzyme cleaner and water, of adherent visible soil, blood, protein substances, microorganisms and other debris from the surfaces, crevices, serrations, joints, and lumens of instruments, devices, and equipment by a manual or mechanical process that prepares the items for safe handling and/or further decontamination (Rutala 2008).
Disinfection	Thermal or chemical destruction of pathogenic and other types of microorganisms. Disinfection is less lethal than sterilisation because it destroys most recognised pathogenic microorganisms but not necessarily all microbial forms (e.g., bacterial spores) (Rutala 2008).
Health‐care associated colonisation	The presence of microorganisms (on skin, mucous membranes, in open wounds, or in excretions or secretions) that are not causing adverse clinical signs or symptoms (Garner 1996). There must be no evidence that the microorganisms were present at the time of admission to the acute care setting.
Hospital	Institution with an organised medical staff which provides medical care to patients (MESH Browser 2009).
Hospital environmental surfaces	Hospital surfaces that generally do not come into direct contact with patients during care. Can be further divided into 'medical equipment surfaces', such as knobs or handles on haemodialysis machines, x‐ray machines, instrument carts, or dental units, and 'housekeeping surfaces', such as floors, walls, bed rails, tabletops or computer keyboards (Sehulster 2003).
Hospital outpatient	Patient admitted to the hospital setting for the purpose of observation, care, diagnosis or treatment without receiving board and room, such as patients attending haemodialysis sessions.
Hospital outpatient clinics	Organised services in a hospital which provide medical care on an outpatient basis (MESH Browser 2009).
Housekeeping surfaces	Environmental surfaces (e.g., floors, walls, ceilings, and tabletops) that are not involved in direct delivery of patient care in health‐care facilities (Sehulster 2003).
Infection	Localised or systemic condition that results from adverse reaction to the presence of an infectious agent(s) or it(s) toxin(s) (Garner 1996).
Inpatient	Person admitted to health facilities which provide board and room for the purpose of observation, care, diagnosis or treatment (MESH Browser 2009).
MRSA decolonisation	Refers mainly to the use of topical agents such as nasal ointment and body wash/shampoo to eradicate/reduce nasal and skin carriage of MRSA (Coia 2006).
Non critical instruments or devices	Medical or surgical instruments or devices that come in contact with intact skin but not with mucous membranes. The risk of infection from use of these devices is low (Rutala 1996).
Nosocomial	Likely to have been acquired during the hospital stay, without any evidence that was incubating or present on admission. However, little consensus exists regarding the precise definition for nosocomial infection or colonization (Cohen 2008).
Rehabilitation centres	Facilities which provide programs for rehabilitating the mentally or physically disabled individuals (MESH Browser 2009).
Residential facilities	Long‐term care facilities which provide supervision and assistance in activities of daily living with medical and nursing services when required. 'Assisted living facilities', 'group homes', 'halfway houses', 'homes for the aged', 'nursing homes' or 'orphanages' are examples of residential facilities (MESH Browser 2009).
Stepped wedge design	Study design where an intervention is rolled‐out sequentially to the trial participants (either as individuals or clusters of individuals) over a number of time periods. The order in which the different individuals or clusters receive the intervention is determined at random and, by the end of the random allocation, all individuals or groups will have received the intervention. Stepped wedge designs incorporate data collection at each point where a new group (step) receives the intervention (Brown 2006).
Sterilisation	Validated process used to render a product free of all forms of viable microorganisms. In a sterilisation process, the presence of microorganisms on any individual item can be expressed in terms of probability. Although this probability can be reduced to a very low number, it can never be reduced to zero (Rutala 2008).
Unit of analysis error	An error made in statistical analysis when the analysis does not take account of the unit of allocation. In some studies, the unit of allocation is not a person, but is instead a group of people, or parts of a person, such as eyes or teeth.  Sometimes the data from these studies are analysed as if people had been allocated individually. Using individuals as the unit of analysis when groups of people are allocated can result in overly narrow confidence intervals. In meta‐analysis, it can result in studies receiving more weight than is appropriate (The Cochrane Collaboration 2005).

Types of participants

We will consider as eligible studies considering the hospital setting, defined for the purposes of this review as an institution with an organised medical staff which provides medical care to patients (MESH Browser 2009). 'Hospital outpatient clinics' will be also eligible. We will exclude the remainder of health care facilities, as defined by the thesaurus of the U.S. National Library of Medicine: 'ambulatory care facilities', 'rehabilitation centres' and 'residential facilities' (see glossary Table 1 for the definition of these terms).

We will consider as eligible studies including the following participants (we define 'participant' as the person in whom the outcome is measured):

1. patients in hospital (of any age). We will consider studies considering 'inpatients' or 'hospital outpatients' (see glossary Table 1 for these terms).

2. any other person who could be responsible for the transmission of MRSA in the hospital setting: any staff working in the hospital setting (healthcare or non‐healthcare professionals) and any carer or visitor.

Types of interventions

We will include studies considering the following experimental and control interventions:

Experimental intervention: decontamination of surfaces in the hospital environment.

• For the purposes of this review, decontamination is defined as a process which removes or destroys contamination so that infectious agents or other contaminants cannot reach a susceptible site in sufficient quantities to initiate infection or any other harmful response (MHRA 2006). The levels of decontamination are either cleaning, cleaning followed by disinfection, or cleaning followed by sterilisation (see the glossary Table 1 for detailed definitions).

• We will consider any form of decontamination of hospital environmental surfaces, irrespective of the type of product used, its concentration, the technique applied, duration, or frequency.

• The combination of two or more methods for decontamination or the decontamination of environmental surfaces in conjunction with any other infection control intervention (for example, patient isolation) will be considered as eligible interventions. The decontamination of carpeting (for example, by vacuuming or steam cleaning) will be also considered as a valid intervention.

• Studies considering the decontamination of bedding and clothing (belonging to patients or staff) will not be eligible. However, any method for the decontamination of hospital curtains and bed screens will be considered as a valid intervention.

The control intervention should consist of one of the following elements:

• no intervention or sham procedure;

• standard practice;

• any other intervention for decontaminating hospital environmental surfaces; or

• any infection control intervention which does not include decontamination of hospital environmental surfaces.

For the purposes of this review we will consider 'hospital environmental surfaces' as hospital surfaces that generally do not come into direct contact with patients during care. Can be further divided into 'medical equipment surfaces', such as knobs or handles on haemodialysis machines, x‐ray machines, instrument carts, or dental units, and 'housekeeping surfaces' (see glossary Table 1), such as floors, walls, tabletops or computer keyboards (Sehulster 2003).

Studies considering the decontamination of 'non critical' instruments or devices (see glossary Table 1) will not be eligible. Examples of 'non‐critical' items are cuffs, stethoscopes, tourniquets, ophthalmoscopes or reflex hammers.

Types of outcome measures

Primary outcomes

• Hospital‐acquired colonisations (measured in inpatients); only in articles reporting an existing screening policy at admission for the health‐care associated pathogen/s considered in the outcome;

• hospital‐acquired infections (measured in patients, staff working in the hospital setting (healthcare or non‐healthcare professionals) or any patients' carer or visitor);

• adverse events in patients, staff or patients' carers or visitors (as considered by the study investigators to be related to the decontamination process).

We will admit any definition used for hospital‐acquired infections and colonisations, as they are not standardised (Cohen 2008). For example, definitions based exclusively in temporal categorisation (‘hospital‐onset infections’) will be admitted, as well as definitions considering also the patient’s clinical history (‘nosocomial infections’).  On the other hand, we will admit any metric for quantifying healthcare acquisition of pathogens, such as incidence rate or incidence density rate.

Secondary outcomes

• Bloodstream infections (see glossary Table 1);

• death from any cause;

• hospital‐acquired infection related mortality;

• length of hospital stay;

• resistance to antibiotics or disinfectants (proportion or rate of isolates of a specific pathogen resistant to a specified antibiotic or disinfectant).

Search methods for identification of studies

Electronic searches

We will search the following electronic databases (without any language or date of publication restriction):

• Cochrane Central Register of Controlled Trials (The Cochrane Library, latest issue);

• Cochrane Wounds Group Specialised Register;

• Cochrane Infectious Diseases Group Specialised Register;

• Cochrane EPOC Group Specialised Register;

• Ovid MEDLINE (1950 to present);

• Ovid EMBASE (1980 to present);

• EBSCO CINAHL (1982 to present);

• Ovid British Nursing Index (1985 to present);

• Database of Abstracts of Reviews of Effects (DARE) (The Cochrane Library, latest issue)

We will use the following search string for CENTRAL, adapted where appropriate for the above mentioned databases:

#1 MeSH descriptor Hospitals explode all trees
#2 MeSH descriptor Hospital Units explode all trees
#3 MeSH descriptor Outpatient Clinics, Hospital explode all trees
#4 MeSH descriptor Patients' Rooms explode all trees
#5 MeSH descriptor Equipment and Supplies, Hospital explode all trees
#6 MeSH descriptor Equipment Contamination explode all trees
#7 MeSH descriptor Health Facilities explode all trees
#8 MeSH descriptor Nursing Homes explode all trees
#9 (#7 AND NOT #8)
#10 hospital*:ti,ab,kw
#11 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #10)
#12 MeSH descriptor Floors and Floorcoverings explode all trees
#13 surface*:ti,ab,kw
#14 (furniture or furnishing*):ti,ab,kw
#15 hand NEXT touch NEXT site*:ti,ab,kw
#16 (#12 OR #13 OR #14 OR #15)
#17 MeSH descriptor Housekeeping, Hospital explode all trees
#18 MeSH descriptor Disinfection explode all trees
#19 MeSH descriptor Infection Control explode all trees
#20 MeSH descriptor Disinfectants explode all trees
#21 MeSH descriptor Detergents explode all trees
#22 MeSH descriptor Decontamination explode all trees
#23 (housekeeping or "house keeping" or hygien* or "sanitary engineering" or sanitation or bundling or antiseptic* or asepsis or biocid* or germicid* or microbicid* or bactericid* or fungicid* or tuberculocid* or virucid* or sanitiz* or sanitis* or decontaminat*):ti,ab,kw
#24 (cleaning or “domestic services” or soap*1 or detergent* or surfactant* or (surface NEXT active NEXT agent*) or cleaner* or mop*1 or vacuum* or (steam NEXT clean*) or (spray NEXT clean*) or (wet NEXT scrub*) or (mechanical NEXT scrub*) or (dry NEXT wip*) or (damp NEXT wash*)):ti,ab,kw
#25 (disinfect* or inactivation or alcohol* or chlorine* or hypochlorite* or aldehyde* or formaldehyde or glutaraldehyde or peroxide* or (peroxygen NEXT compound*) or "benzalkonium chloride" or iodophor* or ortho‐phthalaldehyde or "peracetic acid" or phenolic* or (quaternary NEXT ammonium NEXT compound*) or QUAT or "orthobenzyl parachlorophenol" or "ortho‐benzyl para‐chlorophenol" or (active NEXT oxygen‐based NEXT compound*) or (glycol NEXT derivative*) or alkylamine*):ti,ab,kw
#26 (#17 OR #18 OR #19 OR #20 OR #21 OR #22 OR #23 OR #24 OR #25)
#27 (#11 AND #16 AND #26)

This search string will be adapted where appropriate to search EBSCO CINAHL, Ovid EMBASE and Ovid MEDLINE and these searches will be combined with the methodological search filters developed by the Cochrane EPOC Group (EPOC 2009d).

The following additional electronic resources will be searches:

• ProQuest UMI Dissertation Publishing;

• ISI Conference Proceedings;

• OpenSIGLE

We will search the following clinical trial registers and trials results registers:

• ClinicalTrials.gov;

• Current Controlled Trials (www.controlled‐trials.com);

• International Clinical Trials Registry Platform (www.who.int/trialsearch/);

• IFPMA Clinical Trials Portal (clinicaltrials.ifpma.org/);

• ClinicalStudyResults.org

We will check abstracts presented at the following conferences and available in the corresponding web site (without year restriction):

• Interscience Conference on Antimicrobial Agents and Chemotherapy;

• European Congress of Clinical Microbiology and Infectious Diseases;

• Conference on Antimicrobial Resistance (Bethesda);

• Society for Healthcare Epidemiology of America (SHEA) annual meeting

Searching other resources

We will check the reference lists of all included studies in order to identify relevant papers. We will contact the primary authors of the included studies and relevant reviews in the field to identify further published or non‐published studies eligible for inclusion.The ISI Web of Science will be used to track citations of included studies and other relevant articles. 

Data collection and analysis

Selection of studies

All titles and abstracts of studies identified by the search strategy will be screened independently by two pairs of review authors to assess for eligibility. JLA and JG will screen the first half (based on surname of first author), MG and AMC the other half. If a reliable decision cannot be made based on this information, the full text version will be obtained for further assessment. The full text versions of all potentially eligible studies will be retrieved for definitive assessment of eligibility against the inclusion criteria. JLA and JG will assess the eligibility of the articles generated by the second half of the titles, and MG and AMC the articles generated by the first half. All studies that appear initially to meet our inclusion criteria, but on closer examination fail to, will be detailed in the table of excluded studies and reasons for exclusion will be documented. Any disagreement will be resolved by discussion between the two pairs of review authors. If there is no consensus a third review author (IS or LOC) or the editorial base of the Wounds Group will be consulted.

Data extraction and management

Two review authors will extract data independently from included studies using a data form based in the ORION Statement checklist (Stone 2007), extended with some items of the CONSORT statement for non‐pharmacological interventions (Boutron 2008) and the EPOC Data Abstraction form (EPOC 2007).

We will extract details of participants, setting and inpatients’ characteristics, methods, intervention and control, outcome data, quality criteria and results. We will also try to register the main study design features as proposed by tables 13a and 13b in the section 13.2.2 of the Cochrane Handbook (Reeves 2009).

Interventions in infection control studies usually have several components. For this reason, we will create a graphical depiction of the experimental and control interventions using the Pat Plot tool (Perera 2007). Once created, a PaT Plot is easy to interpret and allows clear comparisons between different arms of a study (CEBM 2009).

Any discrepancy will be resolved by consensus. If there is no consensus a third review author (JLA, IS or LOC) or the editorial base of the Cochrane Wounds Group will settle the discrepancies. JLA will write to study authors to attempt to obtain important missing information or clarification.

Assessment of risk of bias in included studies

At least two review authors will independently assess the risk of bias of each included study. We will use the tools designed by the EPOC group (EPOC 2009c), one for RCTs, Q‐RCTs, CBAs and CChBAs, which is in accordance with the guidelines in the Cochrane Handbook (Higgins 2009a), and another one for ITSs.

For RCTs, Q‐RCTs, CBAs and CChBAs we will consider the following domains:

1. Was the allocation sequence adequately generated?

2. Was allocation adequately concealed?

3. Were baseline outcome measurements similar?*

4. Were baseline characteristics similar? (see Appendix 1 for the list of potential confounders)

5. Were incomplete outcome data adequately addressed?*

6. Was knowledge of the allocated interventions adequately prevented during the study?*

7. Was the study adequately protected against contamination? (in a controlled trial contamination is the inadvertent application of the intervention being evaluated to people in the control group; or the inadvertent failure to apply the intervention to people assigned to the intervention group. Fear of contamination is one motivation for performing a cluster randomised trial).

8. Are reports of the study free of suggestion of selective outcome reporting?

9. Was the study free from other risks of bias?

   1. Was the compliance with the interventions similar?

   2. Were the timing of the outcomes assessments similar?*

*Assessments will be made for each main outcome (or class of outcomes). 

For ITS we will consider the following domains:

1. Was the intervention independent of other changes?

2. Was the shape of the intervention effect pre‐specified?

3. Was the intervention unlikely to affect data collection?

4. Was knowledge of the allocated interventions adequately prevented during the study?*

5. Were incomplete outcome data adequately addressed?*

6. Are reports of the study free of suggestion of selective outcome reporting?

7. Was the study free from other risks of bias (seasonality)?

*Assessments will be made for each main outcome (or class of outcomes). 

Each criterion will be labelled as 'Yes' (meaning low risk of bias), 'No' (high risk of bias) or 'Unclear'. See Appendix 2; Appendix 3 for details of criteria on which the judgements will be based. We will try to obtain this information from the papers but, if there is not enough information to make a judgement, JLA will write to the authors for clarification. Disagreements will be resolved by discussion and consensus, and by consulting a third review author (JLA, IS or LOC) if necessary. Inter‐rater reliability will be assessed using the kappa statistic.

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

For cluster‐randomised trials, we will assess these additional sources of bias: recruitment bias; baseline imbalance in either clusters or individuals; loss of clusters; and incorrect analysis; (Higgins 2009b, Section 16.3.2). Each criterion will be labelled as 'Yes' (meaning low risk of bias), 'No' (high risk of bias) or 'Unclear'. See Appendix 4 for details of criteria on which the judgements will be based.

We will fill out a risk of bias table for each eligible study and we will report the results of assessments of confounders in an additional table, listing the pre‐stated confounders as columns and the studies as rows (Reeves 2009) (see Appendix 1 for the list of potential confounders). Two figures will be also included in the review: a ‘Risk of bias graph figure’ and a ‘Risk of bias summary figure’.

We will assess the overall risk of bias for each outcome (or class of similar outcomes) within each study.

For RCT, Q‐RCT, CBA, CChBA and ITSs, each outcome (or class of outcomes) will be defined as having a ‘low risk of bias’ only if it meets all the domains; as ‘high risk of bias’ if it demonstrates high risk of bias for one or more of them; or an ‘unclear risk of bias’ if it demonstrates unclear risk of bias for at least one key domain without any of them described as ‘high risk of bias’.

Finally, we will incorporate the results of the risk of bias assessment into the review through systematic narrative description and commentary and we will explore the effect of the risk of bias in the meta‐analysis by carrying out sensitivity analysis (see 'Sensitivity analysis').

Measures of treatment effect

We will report study results, organised by type of intervention and study design. All outcome effects will be shown with their associated 95% confidence intervals (CI).

For RCTs and Q‐RCTs, we will report, when possible, the Risk Ratio (RR) for dichotomous data (for example, incidence of hospital‐acquired infections); the Odds Ratio (OR) for counts of rare events and rates (for example, incidence density rate of hospital‐acquired infections); and for continuous data (for example, length of stay) we will use the Mean Difference (MD).

For CBA and CChBAs we will report, when possible, adjusted relative effects. For dichotomous outcomes we will report the RR, adjusted for baseline differences in the outcome measure (i.e. the Risk Ratio post‐intervention/Risk Ratio pre‐intervention). For continuous variables we will use the relative changes, adjusted for 'baseline' differences in the outcome measure (i.e. (the absolute post‐intervention difference between the intervention and control groups ‐ the absolute pre‐intervention difference between the intervention and control groups)/the post‐intervention level in the control group) (EPOC 2009b).

For ITSs we will present, if possible, the results for the outcomes as changes along two dimensions: change in level and change in slope. Change in level is the immediate effect of the intervention and is measured as the difference between the observed level at the first intervention time point and that level predicted by the pre‐intervention time trend. Change in slope is the change in the trend from pre‐ to post‐intervention, reflecting the long term effect of the intervention (Austvoll‐Dahlgren 2008). Studies with an inappropriate analysis of the results will not be re‐analysed.

Unit of analysis issues

We will examine the unit of analysis of the studies looking for potential 'unit of analysis errors' (see glossary Table 1).

Cluster‐randomised controlled trials

We will determine 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 and over narrow confidence intervals (Ukoumunne 1999).

Data will be considered to have been analysed correctly if either:

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

2. the analysis was conducted at the level of the individual, but appropriate statistical correction for the clustering was performed.

If the data analysis is determined to have been performed incorrectly and sufficient information is available, an 'approximately correct analysis' will be performed. If it is not possible, the results of the study will be reported as point estimates of the intervention effect without presentation of any statistical analysis (P values) or confidence intervals and they will not be included in the meta‐analysis (Higgins 2009b).

We will also assess if the unit of allocation has 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 will evaluate whether the sample size has been estimated based on the intra‐cluster correlation co‐efficient (ICC).

Outcome of interest is an event that may re‐occur

If the outcome of interest is an event that may re‐occur (such as health care associated infections), we will assess if count data are treated erroneously as if they are dichotomous data (Deeks 2009).

Additional analysis issues

We will also examine critically the statistical approaches of the included studies.

1. We will examine if the method of analysis of CBA studies accounts for eventual baseline differences of the outcomes (see before 'Measures of treatment effect').

2. We will assess if the statistical approach relating to infection or colonisation outcomes is 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 chi‐squared 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 (Stone 2007).

Dealing with missing data

Missing outcomes data will be assessed and reported. We will contact the authors of the primary studies for missing data and clarification of issues. If we do not obtain this data, it will be clearly documented on the data extraction form.

As far as possible, we will carry out analyses on an intention‐to‐treat principle for all outcomes; i.e. we will attempt to include all participants randomised to each group in the analyses, irrespective of what happened subsequently. The denominator for each outcome in each trial will be the total number of people who had data recorded for the particular outcome in question. We will exclude from the meta‐analysis studies with levels of missing data described during the risk of bias assessment stage as enough to induce clinically relevant bias in the intervention effect estimate.

We will explore the impact in the overall treatment effect of including studies with high levels of missing data by using sensitivity analysis

Assessment of heterogeneity

We will display graphically the results of clinically and methodologically comparable studies and we will assess heterogeneity visually. We will also use the chi‐squared test for identifying heterogeneity (a significant P‐value will be considered for P < 0.10) and the I² statistic (Higgins 2003) for its quantification. I² statistic describes the percentage total variation across studies that is due to heterogeneity rather than chance. We will judge the importance of the observed value of I² depending on the magnitude and direction of effects and the strength of evidence for heterogeneity (moderate to high heterogeneity will be defined as I² ≥ 50%) (Deeks 2009).

Assessment of reporting biases

If sufficient studies are found, we will assess publication bias by means of a funnel plot for each outcome (a simple scatter plot of the intervention effect estimates from individual studies against some measure of each study’s size or precision (Sterne 2009)). Funnel plot asymmetry will be assessed statistically. If there is evidence of asymmetry, publication bias will be considered as only one of a number of possible explanations.

Data synthesis

The outcome measures from the individual trials will be combined in a meta‐analysis to provide a pooled effect estimate if there are enough studies, these are sufficiently similar and described as 'low risk of bias'.

We will not make any attempt to combine data from randomised trials and non randomised studies. Cluster‐randomised trials will be combined with individually randomised trials in the same meta‐analysis. However, we will consider in the sensitivity analysis the possibility of important differences in the effects being evaluated depending on the unit of allocation (see 'Sensitivity analysis').

If no relevant statistical heterogeneity is detected (I² < 50%), we will use a random‐effects model to pool data, although we will assess in the sensitivity analysis the influence of a fixed‐effects model in the effects being evaluated.

In the event relevant statistical heterogeneity is detected or the meta‐analysis is inappropriate for any other reason, we will only undertake a narrative analysis of eligible studies, providing a descriptive presentation of the results, grouped by intervention and study design, with supporting tables.

We will perform the analyses using the Review Mananger 5 (RevMan 2008) statistical package provided by the Cochrane Collaboration and we will present the results with 95% confidence intervals (95% CI).

Subgroup analysis and investigation of heterogeneity

Subgroup analysis will be undertaken as stated below if sufficient numbers of studies are identified.

• Infectious risk of the area*: 'Areas without infectious risk' versus 'general infectious risk areas' versus 'special infectious risk areas'versus 'areas with patients harbouring microbes':

  • Areas without infectious risk: stairways, corridors, administrative areas, offices, dinning rooms, lecture/teaching rooms, engineering rooms.

  • General infectious risk areas: general medical wards, surgical wards, paediatric wards, care of the elderly wards, outpatient departments, radiology, physiotherapy, dialysis units, obstetrics, intensive care/surveillance units and sanitary areas.

  • Special infectious risk areas: operating theatres, surgical procedures rooms, areas used for special intensive care (long‐term ventilated patients (> 24h)), burn units, transplantation units, haemato‐oncology units (e.g., patients undergoing aggressive chemotherapy), HIV units and areas with preterm babies.

  • Areas with patients harbouring microbes in or on their body such that there could be a risk of transmission: for example, isolation units or nursing functional units where aforementioned patients are treated.

*Modified version of the classification by the Robert Koch Institute (Exner 2007).

• We will undertake a subgroup analysis considering whether the intervention was or was not implemented when infection rates were noted to be increasing or to exceed a recognised benchmark.

Sensitivity analysis

If there are sufficient studies the next sensitivity analysis will be undertaken:

1. We will repeat the meta‐analysis to assess the effect of including only studies with allocation to interventions at the group level ('cluster designs').

2. We will repeat the meta‐analysis to assess the effect of including studies with low or unclear risk of bias.

3. We will repeat the meta‐analysis to assess the effect of including studies with high levels of missing data.

4. We will repeat the meta‐analysis to assess the effect of using a fixed‐effects model.

What's new

Date	Event	Description
14 November 2022	Amended	This protocol will not be progressed to review stage.

History

Protocol first published: Issue 8, 2010

Date	Event	Description
18 January 2011	Amended	Contact details updated.
7 September 2010	Amended	Contact details updated.
3 August 2010	Amended	Contact details updated.

Notes

A glossary of terms has been developed see Table 1.

Appendices

Appendix 1. List of potential confounders

1. Case mix                                                                                         

2. Length of stay                               

3. Seasonal effects                                        

4. Strain type and properties of the organism

5. Numbers colonised on admission

6. Patient crowding/bed occupancy

7. Staffing levels

8. Staffing workloads                                            

9. Hand‐hygiene compliance                                          

10. Handwashing agents used                                            

11. MRSA clearance therapy (for studies considering MRSA)

12. Antibiotic consumption                                             

13. Ward closures                                               

14. Staff–patient contact patterns

15. Processing of isolates

16. Screening practice or frequency

This confounders were proposed by Stone 2007 and Cooper 2003 (no systematic review process was done).

Appendix 2. Risk of bias judgement criteria for RCT, Q‐RCT, CBA and CChBA studies

1. Was the allocation sequence adequately generated?

 ‘YES’, low risk of bias. The investigators describe a random component in the sequence generation process such as: referring to a random number table; using a computer random number generator; coin tossing; shuffling cards or envelopes; throwing dice; drawing of lots or minimization (minimization may be implemented without a random element, and this is considered to be equivalent to being random).

‘NO’, high risk of bias. The investigators describe a non‐random component in the sequence generation process. Usually, the description would involve some systematic, non‐random approach (often called ‘quasi‐randomisation’), for example: sequence generated by odd or even date of birth; sequence generated by some rule based on date (or day) of admission; or sequence generated by some rule based on hospital or clinic record number.

Other non‐random approaches happen much less frequently than the systematic approaches mentioned above and tend to be obvious. They usually involve judgement or some method of non‐random categorization of participants, for example: allocation by judgement of the clinician; allocation by preference of the participant; allocation based on the results of a laboratory test or a series of tests; or allocation by availability of the intervention.

‘UNCLEAR’, uncertain risk of bias. Insufficient information about the sequence generation process to permit judgement of ‘Yes’ or ‘No’.

2. Was the allocation adequately concealed?

‘YES’, low risk of bias. Participants and investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.

‘NO’, high risk of bias. Participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias, such as allocation based on: using an open random allocation schedule (e.g. a list of random numbers); assignment envelopes were used without appropriate safeguards (e.g. if envelopes were unsealed or non‐opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; or any other explicitly unconcealed procedure.

 ‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘Yes’ or ‘No’. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement‐ for example if the use of assignment envelopes is described, but it remains unclear whether envelopes were sequentially numbered, opaque and sealed.

3. Were baseline outcome measurements similar?*

‘YES’, low risk of bias. Any of the following:
Patient outcomes were measured prior to the intervention, and no important differences were present across study groups; or
Patient outcomes were measured prior to the intervention, and they were imbalanced but appropriate adjusted analysis was performed (e.g. analysis of covariance).

 ‘NO’, high risk of bias. Important differences were present and not adjusted for in analysis**.

 ‘UNCLEAR’, uncertain risk of bias. If there are no baseline measure of outcome**.

 4. Were baseline characteristics similar? (seeAppendix 1for the list of potential confounders)

‘YES’, low risk of bias. More than 80% of prognostic indicators are reported and similar at baseline or imbalanced but finally controlled for at the design or analysis stage of the study. 

NO’, high risk of bias. There is no report of characteristics in text or tables or there are differences between control and intervention but finally they are not controlled for at the design or analysis stage of the study. Note that in some cases imbalance in patient characteristics may be due to recruitment bias whereby the provider was responsible for recruiting patients into the trial. 

 ‘UNCLEAR’, uncertain risk of bias. If it is not clear in the paper (e.g. characteristics are mentioned in text but no data were presented).

5. Were incomplete outcome data adequately addressed?*

‘YES’, low risk of bias. Any one of the following:

• No missing outcome data;

• Reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias);

• Missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups;

• For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk not enough to have a clinically relevant impact on the intervention effect estimate;

• For continuous outcome data, plausible effect size (difference in means or standardized difference in means) among missing outcomes not enough to have a clinically relevant impact on observed effect size;

• Missing data have been imputed using appropriate methods.

‘NO’, high risk of bias. Any one of the following:

• Reason for missing outcome data likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups;

• For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in intervention effect estimate;

• For continuous outcome data, plausible effect size (difference in means or standardized difference in means) among missing outcomes enough to induce clinically relevant bias in observed effect size;

• ‘As‐treated’ analysis done with substantial departure of the intervention received from that assigned at randomisation;

• Potentially inappropriate application of simple imputation.

 ‘UNCLEAR’, uncertain risk of bias. Any one of the following:

• Insufficient reporting of attrition/exclusions to permit judgement of ‘Yes’ or ‘No’ (e.g. number randomised not stated, no reasons for missing data provided);

• The study did not address this outcome.

6. Was knowledge of the allocated interventions adequately prevented during the study?*

‘YES’, low risk of bias. Any one of the following:

• No blinding, but the review authors judge that the outcome and the outcome measurement are not likely to be influenced by lack of blinding;

• Blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken;

• Either participants or some key study personnel were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias.

‘NO’, high risk of bias. Any one of the following:

• No blinding or incomplete blinding, and the outcome or outcome measurement is likely to be influenced by lack of blinding;

• Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken;

• Either participants or some key study personnel were not blinded, and the non‐blinding of others likely to introduce bias.

‘UNCLEAR’, uncertain risk of bias. Any one of the following:

• Insufficient information to permit judgement of ‘Yes’ or ‘No’;

• The study did not address this outcome.

7. Was the study adequately protected against contamination?

‘YES’, low risk of bias. Allocation was by community, institution or practice and it is unlikely that the control group received the intervention.

‘NO’, high risk of bias. It is likely that the control group received the intervention (e.g. if patients rather than professionals were randomised).

 ‘UNCLEAR’, uncertain risk of bias. It is UNCLEAR if the study was adequately protected against contamination, for example:

• Professionals were allocated within a clinic or practice and it is possible that communication between intervention and control professionals could have occurred (e.g. physicians within practices were allocated to intervention or control);

• Insufficient information to permit judgement of ‘Yes’ or ‘No’.

8. Are reports of the study free of suggestion of selective outcome reporting?.

‘YES’, low risk of bias. Any of the following:

• The study protocol is available and all of the study’s pre‐specified (primary and secondary) outcomes that are of interest in the review have been reported in the pre‐specified way;

• The study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were pre‐specified (convincing text of this nature may be uncommon).

‘NO’, high risk of bias. Any one of the following:

• Not all of the study’s pre‐specified primary outcomes have been reported;

• One or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not pre‐specified;

• One or more reported primary outcomes were not pre‐specified (unless clear justification for their reporting is provided, such as an unexpected adverse effect);

• One or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis;

• The study report fails to include results for a key outcome that would be expected to have been reported for such a study.

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘Yes’ or ‘No’. It is likely that the majority of studies will fall into this category.

9. Was the study free from other risks of bias? (similar compliance with the interventions and similar timing of the outcomes assessments)

‘YES’, low risk of bias.

• The compliance was acceptable in all groups (the compliance with the interventions is acceptable, based on the reported intensity, duration, number and frequency of sessions for both the index intervention and control intervention(s)); and

• The timing of the outcome assessment was similar in all groups*.

‘NO’, high risk of bias. There is at least one important risk of bias. For example:

• The compliance with the interventions is not acceptable in all groups.

• The timing of the outcome assessment was not similar in all groups*: for example, studies with non‐concurrent controls where seasonality is an issue (i.e. if January to June comprises the intervention group and July to December the control group, the 'seasons' could have caused a spurious effect).

‘UNCLEAR’, uncertain risk of bias. Any one of the following:

• It is UNCLEAR if the compliance was acceptable in all groups (insufficient information to permit judgement of ‘Yes’ or ‘No’).

• It is UNCLEAR if the timing of the outcome assessment was similar in all groups*.

*Assessments will be made for each main outcome (or class of outcomes).  

**If ‘UNCLEAR’ or ‘No’, but there is sufficient data in the paper to do an adjusted analysis (e.g. baseline adjustment analysis or Intention to treat analysis) the criteria should be re scored to ‘Yes’.

Appendix 3. Risk of bias judgement criteria for Interrupted time series studies

1. Was the intervention independent of other changes?

‘YES’, low risk of bias. If there are compelling arguments that the intervention occurred independently of other changes over time and the outcome was not influenced by other confounding variables/historic events during study period. If events/variables identified, note what they are.

‘NO’, high risk of bias. If reported that intervention was not independent of other changes in time.

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘Yes’ or ‘No’.

2. Was the shape of the intervention effect pre‐specified?

‘YES’, low risk of bias. If point of analysis is the point of intervention OR a rational explanation for the shape of intervention effect was given by the author(s). Where appropriate, this should include an explanation if the point of analysis is NOT the point of intervention.

‘NO’, high risk of bias. If it is clear that the condition above is not met

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘Yes’ or ‘No’.

3. Was the intervention unlikely to affect data collection?

‘YES’, low risk of bias. If reported that intervention itself was unlikely to affect data collection (for example, sources and methods of data collection were the same before and after the intervention);

‘NO’, high risk of bias. If the intervention itself was likely to affect data collection (for example, any change in source or method of data collection reported).

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘Yes’ or ‘No’.

4. Was knowledge of the allocated interventions adequately prevented during the study?*

‘YES’, low risk of bias. Any one of the following:

• No blinding, but the review authors judge that the outcome and the outcome measurement are not likely to be influenced by lack of blinding

• Blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken

• Either participants or some key study personnel were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias.

‘NO’, high risk of bias. Any one of the following:

• No blinding or incomplete blinding, and the outcome or outcome measurement is likely to be influenced by lack of blinding

• Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken

• Either participants or some key study personnel were not blinded, and the non‐blinding of others likely to introduce bias.

‘UNCLEAR’, uncertain risk of bias. Any one of the following:

• Insufficient information to permit judgement of ‘Yes’ or ‘No’

• The study did not address this outcome.

5. Were incomplete outcome data adequately addressed?*

‘YES’, low risk of bias. If missing outcome measures were unlikely to bias the results. For example:

• There is a follow‐up of discharged patients in the community and the proportion of missing data was similar in the pre‐ and post‐intervention periods or the proportion of missing data was less than the effect size i.e. unlikely to overturn the study result; or

• There is an appropriate analysis of outcome data that explicitly takes account of changing patients LOS. For example: survival analysis (in survival analysis the time until a patient acquires the pathogen is modelled).

‘NO’, high risk of bias. If missing outcome data was likely to bias the results.

‘UNCLEAR’, uncertain risk of bias. If not specified in the paper (do not assume 100% follow up unless stated explicitly).

6. Are reports of the study free of suggestion of selective outcome reporting?

‘YES’, low risk of bias. Any of the following:

• The study protocol is available and all of the study’s pre‐specified (primary and secondary) outcomes that are of interest in the review have been reported in the pre‐specified way;

• The study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were pre‐specified (convincing text of this nature may be uncommon).

‘NO’, high risk of bias. Any one of the following:

• Not all of the study’s pre‐specified primary outcomes have been reported;

• One or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not pre‐specified;

• One or more reported primary outcomes were not pre‐specified (unless clear justification for their reporting is provided, such as an unexpected adverse effect);

• One or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis;

• The study report fails to include results for a key outcome that would be expected to have been reported for such a study.

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘Yes’ or ‘No’. It is likely that the majority of studies will fall into this category.

7. Was the study free from other risks of bias (seasonality)?

‘YES’, low risk of bias. There is no evidence of seasonality being is an issue; the study considers at least 12 monthly data points pre and 12 monthly data points after the intervention.

‘NO’, high risk of bias. There is evidence of seasonality being is an issue: the study does not consider at least 12 monthly data points pre and 12 monthly data points after the intervention (for example, if January to June comprises the pre‐intervention period and July to December the post, could the “seasons’ have caused a spurious effect).

‘UNCLEAR’, uncertain risk of bias. If not specified in the paper.

 *Assessments will be made for each main outcome (or class of outcomes). 

Note: If the ITS study has ignored secular (trend) changes and performed a simple t‐test of the pre versus post intervention periods without further justification, the study will not be included in the review.

Appendix 4. Risk of bias judgement criteria for cluster‐randomised trials

1. Was recruitment bias adequately prevented?

‘YES’, low risk of bias. Individuals were not recruited to the trial after the clusters had been randomised.

‘NO’, high risk of bias. Individuals were recruited to the trial after the clusters had been randomised (the knowledge of whether each cluster is an ‘intervention’ or ‘control’ cluster could affect the types of participants recruited).

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘YES’ or ‘NO’.

2. Were baseline imbalances (in terms of either the clusters or the individuals) adequately addressed?

‘YES’, low risk of bias.

• the randomised groups were similar at baseline; or

• the randomised groups were imbalanced at baseline but finally controlled for at the design (such as using stratified or pair‐matched randomisation of clusters) or analysis stage of the study.

‘NO’, high risk of bias. There were baseline imbalances between the randomised groups, but finally they were not controlled for at the design or analysis stage of the study.

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘YES’ or ‘NO’.

3. Were loss of clusters and participants adequately addressed?

 ‘YES’, low risk of bias.
 ‘NO’, high risk of bias.
 ‘UNCLEAR’, uncertain risk of bias.

See Appendix 2: "Were incomplete outcome data adequately addressed?" for criteria of how we will assess this domain.

4. Was the study analysed by correct statistical methods (i.e. taking the clustering into account)?

‘YES’, low risk of bias. The cluster‐randomised trial was analysed by correct statistical methods, taking the clustering into account. Ways to avoid unit‐of‐analysis errors in cluster‐randomised trials are (see Cochrane Handbbok 16.3.3, Higgins 2009b):

• to conduct the analysis at the same level as the allocation;

• to conduct the analysis at the level of the individual while accounting for the clustering in the data. Such an analysis might be based on a ‘multilevel model’, a ‘variance components analysis’ or a ‘generalized estimating equations (GEEs)’, among other techniques.

‘NO’, high risk of bias. The cluster‐randomised trial was analysed by incorrect statistical methods, not taking the clustering into account. Such analyses tends to create a ‘unit of analysis error’ and produce over‐precise results (the standard error of the estimated intervention effect is too small) and p values that are too small. Although they do not lead to biased estimates of effect, if they remain uncorrected, they will receive too much weight in a meta‐analysis.

‘UNCLEAR’, uncertain risk of bias. Insufficient information to permit judgement of ‘YES’ or ‘NO’.

Contributions of authors

Jesus Lopez‐Alcalde (JLA) conceived the review and coordinated, planned, developed, wrote and edited the protocol.
Stephanie Dancer (SD), Arturo J Martí Carvajal (AMC), Javier Gracia (JG) and Iván Solá (IS) planned, developed and edited the protocol.
Jesus Lopez‐Alcalde (JLA) and Iván Solá (IS) planned and developed the search strategy.
The rest of review authors edited and approved the protocol.

Contributions of editorial base:

Nicky Cullum: edited the protocol; advised on methodology, interpretation and protocol content. Approved the final protocol prior to submission.
Sally Bell‐Syer: coordinated the editorial process. Advised on methodology, interpretation and content. Edited and copy edited the protocol.
Ruth Foxlee: designed the search strategy and edited the search methods section.

Sources of support

Internal sources

• Hospital Universitario de Guadalajara, SESCAM, Spain

• Iberoamerican Cochrane Centre, Spain

External sources

• Agencia de Calidad del Sistema Nacional de Salud, Ministerio de Sanidad y Política Social, Spain

• Cochrane Wounds Group, University of York, UK

• Instituto Ciencias de la Salud, Toledo, Spain

Declarations of interest

No authors have any financial interest in this intervention. One of the authors (Stephanie Dancer) has undertaken a study on cleaning. If included, it will be reviewed, rated, and data extracted by colleagues not involved in the study.

Edited (no change to conclusions)