Summary of findings
Antibiotic resistance is now regarded as a major public health problem. In comparison with infections caused by susceptible bacteria, those caused by multidrug-resistant bacteria are associated with higher incidences of mortality and prolonged hospital stay (de Kraker 2010; de Kraker 2011a; de Kraker 2011b; Wolkewitz 2010). Clostridium difficile infection is another manifestation of the collateral damage caused by antimicrobial prescribing (Davey 2010). Such infections are also associated with increased costs, arising from the need to use more expensive antibiotics as therapy, prolonged hospital stay (de Kraker 2011a) and expenses related to screening and surveillance, eradication regimens and consumables (the gloves, gowns and aprons used to prevent cross-infection). The emergence of multidrug-resistant organisms limits the choice of therapy for patients with hospital-acquired infections and, ominously, for the first time since antibiotics were introduced we are faced with the prospect of not having effective treatment for some patients with bacterial infections (So 2010). A number of reports have proposed a range of measures designed to address the problem of increasing resistance (Behar 2000; EU 2002; Goldmann 1996; House of Lords 1998; House of Lords 2001; Lawton 2000; Shlaes 1997; SMACS 1998). Common to all the recommendations is the challenge to reduce inappropriate antibiotic prescribing, the implication being that antibiotic resistance is largely a consequence of the selective pressures of antibiotic usage and that reducing these pressures by the judicious administration of antibiotics will facilitate a return of susceptible bacteria or, at least, will prevent or slow the pace of the emergence of resistant strains. At the same time, sepsis kills more people annually than myocardial infarction or breast, colon and lung cancer combined (Robson 2008), and delay in effective antibiotic treatment is associated with increased mortality (Daniels 2010; Kumar 2006 ). The term 'antibiotic stewardship' is used to capture the twin aims of ensuring effective treatment of patients with infection and minimizing collateral damage from antimicrobial use (Allerberger 2009; Davey 2010; Dellit 2007; MacDougall 2005).
There is evidence that antibiotic usage in hospitals is increasing, and that over a third of prescriptions are not compliant with evidence-based guidelines (Zarb 2011). In Denmark, antibiotic usage in hospitals increased by 18% between 1997 and 2001 (Muller-Pebody 2004). A similar study carried out in the Netherlands revealed that hospital antibiotic usage between 1997 and 2000 increased by 10.6%. However, more recent data from the Netherland showed that the number of hospital admissions as well as the antibiotic use has increased by 22% from 2003 to 2010. The authors interpreted these results as showing that total use and clinical activities were increasing in parallel. However, they noted that the use of penicillins with extended spectrum and quinolones increased from 2008 to 2011 and that this was not fully explained by increased clinical activity (SWAB 2011). Finally, a survey of 22 US academic centres found that there was a statistically significant increase in total antibacterial use between 2002 and 2006, from a mean of 798 days of therapy (DOTs) per 1000 patient days (PDs) to a mean of 855 DOTs per 1000 PDs (Polk 2007). The European Surveillance of Antimicrobial Consumption (ESAC) has established a method for point prevalence of antibiotic prescribing in hospitals (Amadeo 2010; Ansari 2008) and the 2009 survey included data from 172 hospitals in 25 countries (Zarb 2011). These surveys have revealed important targets for improving the quality of antimicrobial prescribing to hospital inpatients. In the 2009 survey the indication for treatment was not recorded in case notes of 24% of patients and when an indication was recorded it was not compliant with local or national guidelines in 38% of patients. There was also evidence of excessive treatment of community-acquired infections and unnecessary prolongation of surgical antibiotic prophylaxis (Zarb 2011).
What should be done to improve antibiotic stewardship in hospitals? The Infectious Diseases Society of America and the Society of Hospital Epidemiologists of America have recommended measures to improve antibiotic prescribing in hospitals (Dellit 2007). However, the recommendations are based on only a small proportion of the published literature, and the literature that was assessed was not subjected to critical evaluation or systematic review. We have therefore reviewed the literature for evidence of the impact of interventions on the appropriateness of antimicrobial prescribing and on the prevalence of antimicrobial resistance and/or clinical outcome.
This review of interventions intended to improve prescribing of antibiotics to hospital inpatients complements a review of interventions to improve prescribing of antibiotics to patients in ambulatory care (Arnold 2005).
The primary aim is to identify interventions that, alone, or in combination, are effective in improving antibiotic prescribing to hospital inpatients. We have used the term 'antibiotic stewardship' to address two objectives. The first objective is to ensure effective treatment for patients with bacterial infection. The second objective is to provide convincing evidence and information to educate and support professionals and patients to reduce unnecessary use and minimize collateral damage. Collateral damage means the increased risk of infection with antibiotic- resistant bacteria, and antibiotic resistant bacteria, which arises from damage to the normal bacterial flora after antibiotic treatment.
Criteria for considering studies for this review
Types of studies
We included all randomized and nonrandomized controlled trials (RCTs and CCTs), controlled before-after studies (CBAs) and interrupted time series studies (ITSs) (with at least three data points before and after implementation of the intervention).
Types of participants
Healthcare professionals who prescribe antibiotics to hospital inpatients receiving acute care (including elective inpatient surgery). The review excludes interventions targeted at residents in nursing homes or other long-term healthcare settings.
Types of interventions
The following professional interventions in the Effective Practice and Organisation of Care Group (EPOC) scope were included:
- Persuasive interventions: distribution of educational materials; educational meetings; local consensus processes; educational outreach visits; local opinion leaders; reminders provided verbally, on paper or on computer; audit and feedback.
- Restrictive interventions:selective reporting of laboratory susceptibilities, formulary restriction, requiring prior authorization of prescriptions by infectious diseases physicians, microbiologists, pharmacists etc, therapeutic substitutions, automatic stop orders and antibiotic policy change strategies including cycling, rotation and cross-over studies.
- Structural: changing from paper to computerized records, rapid laboratory testing, computerized decision support systems and the introduction or organization of quality monitoring mechanisms.
Studies that were clinical trials comparing the effectiveness of antibiotic treatments (for example intravenous (IV) versus oral administration of antibiotics) were considered invalid for this review.
Types of outcome measures
- Antibiotic prescribing process measures(decision to treat, choice of drug, dose, route or duration of treatment);
- Clinical outcome measures (mortality, length of hospital stay);
- Microbial outcome measure (colonization or infection with Clostridium difficile or antibiotic-resistant bacteria).
Search methods for identification of studies
For this update, we searched the Cochrane Central Register of Controlled Studies (CENTRAL), PubMed, EMBASE in 2006. We used search terms: antibiotics, premedication, guideline, clinical protocols, critical pathways, evidence based medicine, intervention. We also searched the EPOC Register in July 2007 and February 2009 (Appendix 1). The next update of this review will include fully documented search strategies.
Data collection and analysis
Selection of studies
Two authors (EB and PD) reviewed citations and abstracts retrieved in the search to identify all reports that included original data about interventions to change antibiotic prescribing. If either author had any doubt about eligibility, then both authors reviewed the full papers . The authors were not blinded to study author or location. We resolved disagreements by discussion and consensus.
We then excluded studies that had no relevant and interpretable data presented or obtainable. 'Relevant data' was defined as an intervention that included a change in antibiotic treatment for hospital inpatients and at least one of the study's reported outcomes was directly attributable to change in antibiotic treatment. 'Interpretable data' was defined as follows: CBA, CCT or RCT designs had to include sufficient data to estimate effect size with 95% confidence interval (CI) as change in at least one relevant outcome after the intervention. For proportions this was either the numerator and denominator or the risk difference (or risk ratio or odds ratio). For continuous variables this was either the mean plus standard deviation or standard error, plus number in each group. ITS studies had to include a clearly defined intervention point.
We did not exclude studies because of high risk of bias.
We reached all decisions about minimum methodological criteria by consensus between the authors, and had them confirmed by the review editor, Lisa Bero.
Data extraction and management
Two review authors independently performed data abstraction using a template which included information on: study design, type of intervention, presence of controls, type of targeted behaviour, participants, setting, methods (unit of allocation, unit of analysis, study power, methodological quality, consumer involvement), outcomes, and results.
Explanation of terms used to describe interventions
We applied the EPOC definitions for each intervention, with additional detail relevant to the context of this review. The persuasive interventions considered were:
- Dissemination of educational materials in printed form or via educational meetings;
- Audit and feedback;
- Educational outreach (academic detailing or review and recommend change).
Restrictive interventions correspond to the EPOC category of 'financial and healthcare system changes' used in the Cochrane review of interventions to improve antibiotic prescribing in ambulatory care (Arnold 2005). These interventions involve a change to the antibiotic formulary or policy implemented through an organizational change that restricts the freedom of prescribers to select some antibiotics. We identified four distinct types of restrictive interventions:
- Compulsory order form - prescribers had to complete a form with clinical details to justify use of the restricted antibiotics;
- Expert approval - the prescription for a restricted antibiotic had to be approved by an Infection specialist or by the Head of Department;
- Restriction by removal - a restrictive policy was imposed in target wards, units or operating theatres, for example by removing restricted antibiotics from drug cupboards;
- Review and make change - the difference between this intervention and review and recommend change (educational outreach) is that the reviewer changed the prescription rather than giving health professionals either a verbal or written recommendation that they should change the prescription.
In addition some studies included automatic stop orders (termination of prescriptions after a specified interval unless authorization was obtained to continue) but automatic stop orders were never used as the main intervention.
None of the restrictive interventions in our review included financial incentives or penalties.
In this category we included the introduction of new technology for laboratory testing or changes to laboratory turnaround time that required substantive changes to the work patterns of the microbiology laboratory, or computerized decision support that required substantive changes to the hospital’s information systems.
Assessment of the impact of interventions
We have used meta-analysis to make the following comparisons in assessing the impact of interventions on antibiotic prescribing and outcomes:
Comparison 1: effect of persuasive versus restrictive interventions on antibiotic prescribing;
Comparison 2: effect of persuasive versus restrictive interventions on microbial outcomes;
Comparison 3: effect of interventions intended to increase effective antibiotic treatment versus no intervention on clinical outcomes;
Comparison 4: effect of interventions intended to reduce unnecessary antibiotic treatment versus no intervention on clinical outcomes.
Assessment of risk of bias in included studies
We applied the 2009 revised EPOC risk of bias criteria to all papers in the review, including articles in the 2003 review (Cochrane EPOC 2013). We scored each study for risk of bias as 'Low' if all criteria were scored as 'Done', 'Medium' if one or two criteria were scored as 'Unclear' or 'Not Done', and 'High' if more than two criteria were scored as Unclear' or 'Not Done'.
The EPOC group criteria for a reliable primary outcome measure include "When there were two or more raters with at least 90% agreement or kappa greater than or equal to 0.8". However, kappa values may be as low as 0.39 for composite quality indicators even when data abstraction is carried out by trained abstractors, so the inter-rater reliability is likely to be the best possible (Scinto 2001). The key issue is whether or not the actual agreement is sufficient for the application of the quality indicator, so for composite measures such as quality or timing of antibiotic therapy we accepted kappa values as low as 0.6 (Marwick 2007; Williams 2006).
We applied three additional criteria to studies with microbial risk of outcome, based on the ORION statement: Guidelines for transparent reporting of outbreak reports and intervention studies of nosocomial infection (Stone 2007, http://www.idrn.org/orion.php). The most important of these is the distinction between planned and unplanned intervention. An unplanned intervention is made in response to a problem, which makes interpretation of the effect of the intervention difficult because of regression to the mean, which is the natural tendency for extreme results to be followed by a return to normal. Regression to the mean is an important risk of bias for any unplanned intervention but is a particular problem for studies of infection because of the shape of the epidemic curve (Cooper 2003; Davey 2001). A classic example is the 1854 cholera epidemic in Golden Square, London, when the number of deaths per day fell from 140 to 20 in five days without any intervention (Davey 2001). The additional Microbial Outcome Criteria were:
- Case definition: score as DONE if there is a clear definition either of infection or of colonization and there were no major changes in laboratory diagnostic methods during the study period.
- Planned intervention: score as DONE if the intervention was planned to reduce endemic rates of colonization or infection and was not implemented in response to an outbreak.
- Other infection control measures: score as DONE if infection control practices (hand hygiene, gowning or other personal protection) and isolation or cohorting policies are described and there were no changes coincident with the intervention to change antibiotic prescribing.
In the risk of bias tables these criteria are listed under 'other bias'. In the EPOC risk of bias tables, the microbial criteria count in two of the criteria: 'intervention independent of other changes' and 'other biases'. In the results tables of Microbial Outcomes (17a-d) we have included an assessment of microbial risk of bias based on the ORION criteria: low has no risks, medium has one and high has two or three microbial risks of bias.
Measures of treatment effect
Data are reported in natural units in the Characteristics of included studies tables and the Results section. We calculated the effects of interventions by study designs. When there is more than one study of the same study design, we calculated the effect size by taking the median value across studies. We have divided outcomes into four main groups: prescribing, clinical, microbiological and financial. 'Prescribing' includes the decision whether or not to prescribe an antibiotic, choice of drug, dosage, route of administration, dosing interval and duration of treatment. 'Clinical' includes length of hospital stay, incidence of readmissions, mortality and the occurrence of specific infections defined by clinical diagnosis (e.g. wound infection) without information about microbiological cause. 'Microbial' includes incidence of infection caused by specific bacteria (e.g. Clostridium difficile and colonization with or infection caused by antimicrobial-resistant bacteria). One study (Micek 2004) used the number of infections in the intensive care unit as a balancing measure of unintended consequences of a change in antibiotic policy. We have not included this as a microbial outcome. 'Financial' includes studies that provide information about both the cost of developing or implementing the intervention and about savings arising from the intervention.
For the included RCT or CBA studies, when possible we report pre-intervention and postintervention percentages for both study and control groups, and calculate the absolute change from baseline with 95% confidence intervals (CIs).
We examined the methods of analysis of ITS data critically. The preferred method is a statistical comparison of time trends before and after the intervention. If the original paper did not include an analysis of this type, we extracted the data presented in tables or graphs in the original paper and used them to perform new analyses where possible. We used segmented time-series regression analysis to estimate the effect of the intervention whilst taking account of time trend and autocorrelation among the observations. We obtained estimates for regression coefficients corresponding to two standardised effect sizes for each study: a change in level and a change in trend before and after the intervention. A change in level was defined as the difference between the observed level at the first intervention time point and that predicted by the pre-intervention time trend. A change in trend was defined as the difference between post- and pre-intervention slopes (Ramsay 2003). A negative change in level and slope indicates an intervention effect in terms of a reduction in infection rates. We evaluated the direct effect of the intervention using results reported one month after the intervention started. We also reported the level effects at six months, and yearly thereafter when possible. We standardized the results of some ITS studies so that they were on the same scale (per cent change in outcome), thereby facilitating comparisons of different interventions. To do this, we used the change in level and change in slope to estimate the effect size with increasing time after the intervention (one month, six months, one year, etc) as the per cent change in level at each time point. We did not extrapolate beyond the end of data collection after the intervention. We anticipated that the eligible studies would exhibit significant heterogeneity, due to variations in target clinical behaviours, patient and provider populations, methodological features, characteristics of the interventions, and the contexts in which they were delivered. To address the source of variation in results due to the use of restrictive or persuasive interventions, we undertook a random-effects meta-regression analysis on study-level summary effect size at each time point.
We assessed the impact of interventions on microbial outcomes if the study provided reliable data about colonization or infection with Clostridium difficile or with antibiotic-resistant bacteria. We did not include microbial outcomes for studies that estimated the future impact of their intervention based on modelling (Paul 2006) or that used clinical definitions of infection that did not distinguish between resistant and sensitive bacteria (Micek 2004; Singh 2000).
We assessed the impact of interventions on clinical outcome for studies that provided reliable data about mortality or length of hospital stay. We did not include clinical outcomes for studies that estimated the impact of their intervention based on modelling (Barlow 2007).
Unit of analysis issues
If an RCT had not taken into account the effect of clustering in the analysis, we stated this in the risk of bias assessment but did not attempt re-analysis as the intervention and outcomes measured in the studies with unit of analysis errors differed from the studies in the meta-analyses. We therefore expected that the impact of unit of analysis issues would be minimal in this review, given that the evidence was primarily from ITS studies.
The results for RCT, CBA and ITS studies were analyzed separately, and qualitatively described if possible. For the RCT data, if no significant heterogeneity was present (I² < 70%) (Deeks 2011), a standard meta analysis approach using the Review Manager 5 data analysis programme was utilized to perform meta-analysis of binary (e.g. mortality) and continuous (e.g. length of stay) outcomes. If an RCT study had a unit of analysis error the study was excluded in a sensitivity analysis. We did not intend to formally meta-analyze the ITS studies, since we anticipated extreme heterogeneity.
When we found significant heterogeneity, we did not meta-analyze the results, but presented them as the median effect (interquartile range, (IQR)).
To investigate potential reasons for heterogeneity, we performed meta-regression of ITS studies to compare the results of persuasive and restrictive interventions (Comparison 4). RCTs were not involved in the meta-regression because in the event the RCTs did not provide usable data for this comparison. The meta-regression was performed using standard weighted (by standard error of estimate) linear regression (see Cochrane Handbook). All differences were expressed as: (persuasive - restrictive).
We used Stata 11 for all statistical re-analyses and meta-regressions and Review Manager 5 for all data synthesis.
Description of studies
Results of the search
In this update, searching for literature to the end of 2006, we found 50 studies that were published prior to 2003 but were missed in the search for the previous version of the review. The combined results of both literature searches are described in the study flow diagram (Figure 1).
|Figure 1. Study flow diagram.|
The Cochrane EPOC Checklist was changed in January 2007 with the addition of the requirement for CBA studies to have at least two intervention and control sites. In the review update we have applied this new criterion to all studies and have eliminated 23 studies, of which 19 were included in the previous review (Barenfanger 2001; Bendall 1986; Bond 2005; Clapham 1988; Cordova 1986; Covinsky 1982; Eron 2001; Girotti 1990; Gyssens 1996; Herfindal 1983; Herfindal 1985; Khanderia 1986; Ludlam 1999; Parrino 1989; Przybylski 1997; Thornton 1991; Weingarten 1996; Weller 2002; Witte 1987) and four were published after 2003 (Capelastegui 2004; Martinez 2006; Ritchie 2004; von Gunten 2005).
There were 89 studies listed in the Characteristics of included studies table. 56 were ITSs (of which four are controlled ITS studies (CITS): Barlow 2007; Charbonneau 2006; May 2000; Weinberg 2001). 20 were RCTs, 5 were CBAs, 2 were CCTs, 1 was a cluster-CCT and 5 were cluster-RCTs. Full details are given in the Characteristics of included studies table. The 89 studies report 95 interventions with reliable data about at least one outcome. Two studies report two interventions (Mol 2005; Perez 2003) and one study reports five interventions (Fridkin 2002).
Geographical Location of study
Fifty-two studies were from North America. The remaining 37 were from Europe (29, includes Israel), the Far East (3), South America (3) and Australia (2). There were two multinational studies (Franz 2004 took place in five countries: Australia, Austria, Belgium, Germany, Sweden; Paul 2006 took place in three countries: Germany, Israel, Italy). The number of studies by country (including the countries in the two multinational studies) is: Australia (3), Austria (1), Belgium (1), Brazil (1), Canada (4), Colombia (2), France (2), Germany (2), Hong Kong (1), Israel (2), Italy (1), Netherlands (6), Norway (1), Spain (2), Sweden (1), Switzerland (3),Thailand (2), UK (12) and USA (48).
Number of Hospital
A total of 69 (77%) studies were conducted in one hospital, 5 studies (6%) in two hospitals, 6 studies (7%) in 3 to 9 hospitals and 9 studies (10%) in ten or more hospitals.
The aim of the interventions was to optimize therapy either by (a) reducing the amount of antibiotic prescribed where this was considered excessive, or (b) increasing effective treatment by increasing the amount of antibiotic prescribed or improving the timing of administration where these were considered suboptimal. Of the 95 interventions, 79 aimed to decrease excessive antibiotic use, 11 aimed to increase effective treatment and 5 aimed to reduce inappropriate antibiotic use but did not distinguish between excessive or ineffective use (Bouza 2004; Bruins 2005; Burton 1991; Doern 1994; Trenholme 1989).
Nature of Intervention
Most interventions (87/95, 91%) were classified as professional, of which 39 were persuasive and 28 included at least one restrictive component. The remaining interventions were structural.
Target of Intervention
Most of the interventions (80/95, 84%) targeted the choice of antibiotic prescribed (drug selected, timing of first dose or route of administration). The remaining 15 interventions aimed to change exposure of patients to antibiotics by changing the decision to treat or the duration of treatment.
Six studies (Christ-Crain 2004; Christ-Crain 2006; Foy 2004; Franz 2004; Weinberg 2001; Wyatt 1998) targeted the decision to prescribe antibiotics. Three aimed to decrease the percentage of patients who received therapeutic antibiotics (Christ-Crain 2004; Christ-Crain 2006; Franz 2004) and three aimed to increase the percentage of patients who received antibiotic prophylaxis for surgery (Foy 2004; Weinberg 2001; Wyatt 1998).
Nine studies (Berild 2002; Fine 2003; Landgren 1988; Micek 2004; Oosterheert 2005; Senn 2004; Singh 2000; Van Kasteren 2005; Zanetti 2003) targeted the duration of antibiotic treatment or prophylaxis. Six aimed to decrease duration of therapeutic antibiotics (Berild 2002; Fine 2003; Micek 2004; Oosterheert 2005; Senn 2004; Singh 2000), two aimed to decrease duration of antibiotic prophylaxis for surgery (Landgren 1988; Van Kasteren 2005) and one aimed to increase duration of antibiotic prophylaxis for surgery (Zanetti 2003).
Deliverer of intervention
Of the 95 interventions, 37 (39%) were designed and delivered by a multidisciplinary team, 31 (33%) by specialist physicians (Infectious Diseases or Microbiology), 19 (20%) by pharmacists and 8 (8%) by department physicians (e.g. Department of Medicine or Surgery). The proportion of interventions that involved a multidisciplinary team is much higher in studies published from 2003 (11/21, 52%), compared with those published before 2003 (26/74, 35%).
We excluded 29 studies from the review because they did not contain relevant or interpretable data (1 CBA, 11 RCTs, 3 CCTs and 11 ITSs) or were secondary publications (N = 3). Studies that did not contain relevant data were interventions that included antibiotic prescribing but did not provide data to assess the impact of the interventions or outcomes of interest. Studies that did not contain interpretable data were ITS designs with no clear point in time for the intervention, or RCTs with unacceptable selective reporting of results. See Characteristics of excluded studies for details of each study.
Risk of bias in included studies
Eighteen (20%) of the studies had low risk of bias, 31 (35%) studies had medium risk of bias and 40 (45%) had high risk of bias.
All five CBA studies had high risk of bias. High risk of bias was more common in CCTs, RCTs or CRCTs (22/28, 79%) than in ITS or CITS (13/56, 23%) (Figure 2). All 18 studies with low risk of bias were CITS or ITS (Figure 2) High risk of bias in CCTs, RCTs or CRCTs was much more likely in studies with two or fewer hospitals (19/22, 86%) versus three or more hospitals (3/6, 50%). There were only three ITS studies in more than two hospitals and all had medium risk of bias (Charbonneau 2006; Van Kasteren 2005; Wilson 1991).
|Figure 2. Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.|
The three RCTs in two or fewer hospitals with medium risk of bias were Christ-Crain 2004, Christ-Crain 2006 and Senn 2004. The interventions were dissemination of laboratory test results (Christ-Crain 2004; Christ-Crain 2006) and a mailed questionnaire (Senn 2004). Because these interventions were targeted at doctors who were managing specific patients, the risks of allocation or contamination bias were relatively low compared with the other RCTs of interventions in one or two hospitals.
Most of the RCTs had high risk of selection bias (Figure 2). The only RCTs that had low risk of selection bias were either cluster-RCTs (e.g. Paul 2006) or structural interventions, for which concealment of allocation is relatively straightforward.
Most of the RCTs also had high risk of performance and detection bias (Figure 2).
Other potential sources of bias
Most RCTs did not provide information about baseline outcome (Figure 2). The importance of this risk of bias is illustrated by one study in which the intervention was a computer-generated reminder in the operating theatre about giving additional doses of antibiotic prophylaxis for prolonged operations (Zanetti 2003). The results show an increase in the use of additional doses and a reduction in wound infection in the control group in comparison with baseline. The authors attribute this result to contamination during development (surgeons were aware of the planned change) and implementation (surgeons who operated in the intervention theatre also operated in other theatres).
Effects of interventions
Outcomes of intervention
For all outcomes we have included only data that are interpretable according to Cochrane EPOC criteria. Eighty interventions provide valid data about prescribing outcomes, 25 about clinical outcomes, 19 about microbiological outcomes and 10 about financial outcomes (the total adds up to more than 95 because some studies report more than one outcome per intervention).
Impact of persuasive interventions on prescribing outcomes
We report results as change in the direction of the intended effect, so a negative sign indicates that change in prescribing was in the opposite direction to the intended effect.
Overall, for the persuasive interventions, the median (interquartile range) change in antibiotic prescribing was 42.3% for the interrupted time series studies (ITSs), 31.6% for the controlled interrupted time series studies (CITSs), 17.7% for the controlled before-after studies (CBAs), 3.5% for the cluster-randomized controlled trials (CRCTs) and 24.7% for the randomized controlled trials (RCTs).
Fridkin 2002 reported on the impact of five interventions in different hospitals, three persuasive (educational materials, meetings, audit and feedback) and two restrictive (expert approval, restriction by removal). These are reported separately in Table 1; Table 2; Table 3.
Perez 2003 reported one persuasive intervention (reminders) in the same article as a restrictive intervention (compulsory order form). These interventions were both used in the same hospital but were targeted at different behaviours and are reported separately ( Table 4; Table 5).
Dissemination of educational materials in printed form or via educational meetings (six interventions)
See Table 1. Five studies evaluated six interventions that used dissemination of educational materials as the main component (Fridkin 2002; May 2000; Stevenson 1988; Wilson 1991; Wyatt 1998). Of the five studies, one was a CRCT (Wyatt 1998), with an effect size of -3.1%; two studies were ITSs (Stevenson 1988; Wilson 1991), with a median effect size of 10.6%; one study was a CITS (May 2000), with an effect size of 42.5%; and two were CBAs (Fridkin 2002), with a median effect size of 16.1%. The findings had a high degree of clinical heterogeneity. All of the interventions showed a positive result except for the CRCT.
Reminders (eight interventions)
See Table 4. Eight studies evaluated eight interventions. All the interventions were associated with change in prescribing of at least 5% in the intended direction. Three of the studies were RCTs (Senn 2004; Shojania 1998; Zanetti 2003), with a median effect size of 27.4%. Five studies were ITSs (Avorn 1988; Halm 2004; Hulgan 2004; Madaras-Kelly 2006; Perez 2003), with a median effect size of 20%. The findings had a high degree of clinical heterogeneity.
Seven (87.5%) of the eight interventions were multifaceted, with additional educational materials (seven studies) and educational meetings or both (four studies).
Audit and feedback (nine interventions)
See Table 6. Nine studies evaluated nine interventions. Foy 2004 was a CRCT, with an effect size of 3.5%. Four of the studies were ITSs (Berild 2002; Kumana 2001; Mol 2005; Van Kasteren 2005), with an effect size of 32.7%. Two studies were CITSs (Barlow 2007; Weinberg 2001), with a median effect size of 24.3%. Two studies were CBAs (Chu 2003; Fridkin 2002), with a median effect size of 7.5%. The findings had a high degree of clinical heterogeneity.
Two studies reported no significant impact of audit and feedback, but both had design flaws. Fridkin 2002 reported that “evaluating periodic drug use” was an intervention to reduce vancomycin in 19 hospitals but provided no information about feedback of data to prescribers. The level of the intervention is described as hospital-wide rather than ICU-specific, with the implication that there was no feedback to ICU staff about their use of vancomycin. In Foy 2004 there was likely to be a ceiling effect because compliance with the guideline was very high (96.5%) in the control group.
All nine interventions were multifaceted with additional: educational materials (all interventions) and reminders (Barlow 2007; Kumana 2001). Audit and feedback was also an additional component in one study of review and recommend change (Abramowitz 1982) and in one restrictive intervention that used removal by restriction as the main component (Richards 2003).
Educational outreach (22 interventions)
See Table 2. There were 22 studies evaluated 22 interventions. Burton 1991 was not included in Table 2 because the effect size was measured as difference in peak aminoglycoside concentration, which was higher in the intervention group (5.3 versus 4.3 mg/l control, P = 0.001).
Most of the interventions in Table 2 (20/21, 95.2%) were associated with change in prescribing of at least 5% in the intended direction. Ten of the studies were RCTs including one CRCT (Bailey 1997; Bouza 2004; Dranitsaris 2001; Fine 2003; Fraser 1997; Gums 1999; Micek 2004; Naughton 2001; Solomon 2001; Walker 1998); the median effect size was 25%. Ten studies were ITSs (Abramowitz 1982; Adachi 1997; Ansari 2003; Hess 1990; Lee 1995; McLaughlin 2005; Mol 2005; Patel 1989; Richardson 2000; Skaer 1993), with a median effect size of 46.3%. Landgren 1988 was a CBA, with an effect size of 20%. The findings had a high degree of clinical heterogeneity.
However, three ITS studies reported large effect sizes (48.7 to 52.7%) that were not statistically significant by segmented regression analysis (McLaughlin 2005; Richardson 2000; Skaer 1993). Only one intervention (Bailey 1997, an RCT design) was completely ineffective, with a 9.8% increase in duration of intravenous antibiotics when the intended effect was a decrease.
One ITS study evaluated the incremental effect of academic detailing on audit and feedback (Mol 2005). Academic detailing was also used as an additional component in two ITS studies of restrictive interventions with compulsory order forms (Belliveau 1996; Salama 1996) and in one restrictive intervention with expert approval (McElnay 1995). Review and recommend change was also used as an additional component in one restrictive intervention (Inaraja 1986). Bouza 2004 directly compared a written recommendation in the patients' case notes with the written recommendation plus a direct conversation with the patient's physician and found that both interventions were similarly effective. Walker 1998 commented on the difficulty in making direct personal contact with prescribers at district hospitals.
Impact of restrictive interventions on prescribing outcomes
Overall, the restrictive interventions had a median effect size of 34.7% for the interrupted time series designs, 17.1% for the controlled before-after designs and 40.5% for the randomized controlled trials.
Compulsory order forms (five studies)
See Table 5. Five studies evaluated five interventions. All the studies were ITSs (Belliveau 1996; Perez 2003; Saizy-Callaert 2003; Salama 1996; Sirinavin 1998). Three (60%) reported interventions that were associated with change in prescribing of at least 5% in the intended direction. However, the findings had a high degree of clinical heterogeneity. The median effect size was 7.3% with an interquartile range of -0.1 to 28.2% ( Table 5).
One compulsory order form intervention was completely ineffective at one year (Saizy-Callaert 2003). One intervention was associated with an initially significant reduction in vancomycin use, but this then reversed so that the net effect one year after the intervention was an increase in use (Belliveau 1996). In Perez 2003 the same intervention was associated with completely different effects on different drug groups in the same hospital.
All the interventions were multifaceted with additional: educational materials (four), educational meetings (five), reminders (four) and academic detailing (two).
Expert approval (nine studies)
Table 7.reports results on eight interventions on the effect of introducing expert approval and seven (87%) were associated with change in prescribing of at least 5% in the intended direction. Seven of the studies were ITSs (Huber 1982; Lautenbach 2003; McElnay 1995; McGowan 1976; Suwangool 1991; Woodward 1987; Young 1985), with a median effect size of 24.1%. Fridkin 2002 was a CBA, with an effect size of -2.8%. The findings had a high degree of clinical heterogeneity.
The ninth expert approval study (Himmelberg 1991) reported on the effect of removal of the need for expert approval, which our re-analysis showed that it was associated with a 162.2% increase in use of the nine previously restricted drugs (95% CI 97.7 to 226.6%), change in level P = 0.001, and change in slope P = 0.45. This study did not provide information about the effectiveness of the original restriction so has not been included in Table 6 or in the calculation of median effect.
Four (44%) of the expert approval interventions were multifaceted with additional educational materials or meetings (four studies), stop order (one study) and academic detailing (one study Table 7). Himmelberg 1991 was not multifaceted.
Removal by restriction (eight studies)
See Table 3. Eight included studies evaluated eight interventions. Removal by restriction was associated with large changes in the intended direction in all eight studies. Seven of the studies were ITSs (Bradley 1999; Everitt 1990; Inaraja 1986; McNulty 1997; Mercer 1999; Richards 2003; Toltzis 1998), with a median effect size of 60.7%. Fridkin 2002 was a CBA, with an effect size of 37%. The findings had a high degree of clinical heterogeneity. Of the three ITS designs with data at two time points, two showed sustained intervention effects (Richards 2003; Toltzis 1998), but one showed a transient effect (McElnay 1995). Six (75%) of the interventions were multifaceted with: additional educational materials or meetings (five studies), reminders (three studies), stop order (one study) or educational outreach (two studies).
Review and make change (four studies)
See Table 8. Four included studies evaluated four interventions. Two were RCTs (Borer 2004; Singh 2000), with a median effect size of 40.5%. Two were ITSs (Bunz 1990; Gupta 1989), with a median effect size of 94.3%. Review and make change was associated with large changes in the intended direction in all four studies. The findings had a high degree of clinical heterogeneity. None of these studies provided data at more than one time point.
Of the four studies that used review and make change as the main method of dissemination, two (50%) were multifaceted with additional: educational materials (two studies), educational meetings (two studies), and reminders (two studies)
Impact of structural interventions on prescribing outcomes (eight studies)
The structural interventions had a median effect of 13.3% for the RCTs and 23.6% for the cluster-RCTs.
See Table 9. Six studies were RCTs (Bruins 2005; Christ-Crain 2006; Doern 1994; Franz 2004; Oosterheert 2005; Trenholme 1989), and two were CRCTs (Christ-Crain 2004; Paul 2006). Eight (89%) of nine structural interventions were associated with change in prescribing of at least 5% in the intended direction. For the RCTs, the median effect size was 13.3% with an interquartile range of 7.7% to 13.8%; for the cluster-RCTs, the median effect was 23.6% with an interquartile range of 15.9% to 31.2% ( Table 9).
Three structural interventions introduced new tests for inflammatory markers (Christ-Crain 2004; Christ-Crain 2006; Franz 2004), which were associated with 13.5% to 38.8% reduction in the percentage of patients treated with antibiotics. These are the only interventions in this review that achieved this outcome. The other structural interventions introduced rapid microbiology reporting (Bruins 2005; Doern 1994; Trenholme 1989), a new polymerase chain reaction (PCR) test for detecting viruses or atypical bacteria (Oosterheert 2005), and a computerized decision support system (Paul 2006). Only one of these interventions was associated with reduction in exposure to antibiotics by discontinuing treatment earlier than originally planned but the effect was small (3.4% absolute reduction) and not statistically significant (Oosterheert 2005). Two of the rapid microbiology reporting interventions also included educational outreach. In Bruins 2005, same day delivery of a written, individual patient report to the ward had no additional impact over telephone reporting. Trenholme 1989 used educational outreach (a telephone consultation between an infectious diseases (ID) fellow and the prescriber) in both the intervention and control arms, so the intervention effect can be attributed to the microbiology results being available 24 hours earlier in the intervention arm. All eight structural interventions were multifaceted because they also included persuasive components: educational materials (five studies), reminders (four studies) or educational outreach (two studies).
Effect of interventions on microbial outcomes (21 studies)
For all interventions the intended effect was a decrease in the microbial outcome. A total of 23 microbial outcomes were reported by 21 studies (Results Table 10; Table 11; Table 12): Carling 2003 reported four microbial outcomes but we have only included three (Clostridium difficile infections, infection with antibiotic-resistant gram-negative bacteria and methicillin-resistant Staphylococcus aureus (MRSA) infections). This study also reported on vancomycin-resistant enterococci (VRE) but there were no VRE infections until three years after the intervention began. The appearance of VRE infections in the hospital was attributed to transfer of colonized patients from other hospitals (Carling 2003).
Clostridium difficile infections (Five studies)
See Table 10. Five studies evaluated five interventions reported Clostridium difficile infections. All of the included studies were ITSs (Carling 2003; Climo 1998; Khan 2003; McNulty 1997; Pear 1994), showing a median effect size of 68%. All reported change in the intended direction by at least 15% and four by at least 50%. However, only McNulty 1997 had reliable data about intervention impact on prescribing. This study reported the largest intervention effect on Clostridium difficile infection but this was not statistically significant, probably because the study only had seven pre-intervention points. Only two of the studies had low risk of bias and these reported the smallest intervention effect on Clostridium difficile infection (Carling 2003; Khan 2003).
Antibiotic-resistant gram-negative bacteria (Nine studies)
See Table 11. Nine studies evaluated nine interventions reporting colonization or infection with antibiotic-resistant gram-negative bacteria. Seven were ITSs (Calil 2001; Carling 2003; de Champs 1994; Gerding 1985; Landman 1999; Leverstein 2001; Meyer 1993), with a median effect size of 47%. de Man 2000 was a CCCT, with an effect size of 68%. Toltzis 2002 was a CCT, with an effect size of -39%.
Although Toltzis 1998 found that cycling of antibiotics was associated with an increase in resistant gram-negative bacteria, the other eight studies all reported at least a 25% reduction in resistant gram-negative bacteria, but confidence intervals were wide and the effects were not statistically significant in two studies (Gerding 1985; Landman 1999). Moreover, none of the studies had reliable data about intervention impact on prescribing, and only two studies had low microbial risk of bias (Carling 2003; de Man 2000).
Antibiotic-resistant gram-positive bacteria (Seven studies)
See Table 12. Seven studies evaluated seven interventions reporting colonization or infection with antibiotic-resistant gram-positive bacteria. Six were ITSs (Bradley 1999; Carling 2003; Charbonneau 2006; Lautenbach 2003; Madaras-Kelly 2006; May 2000), with a median effect size of 24%. Fridkin 2002 was a CBA, with an effect size of 13.2%.
Six studies reported a statistically significant intervention effect with at least 10% difference in resistance between intervention and control groups. Moreover five studies included reliable data about intervention effects on antibiotic prescribing.
Madaras-Kelly 2006, with low microbial risk of bias, reported that a 50% statistically significant reduction in levofloxacin use (Table 2) was associated with a 21% statistically significant reduction in MRSA infections. Two other interventions also aimed to reduce MRSA infections by reducing fluoroquinolone use, but neither provided reliable data about antibiotic prescribing (Carling 2003; Charbonneau 2006).
Bradley 1999, with low microbial risk of bias, reported that a 61% reduction in ceftazidime use was associated with a statistically significant 25% reduction in vancomycin-resistant enterococci (VRE). However, the impact on ceftazidime prescribing had wide confidence intervals and was not statistically significant ( Table 3).
Three studies reported that reduction in vancomycin use was associated with reduction in VRE (Fridkin 2002; Lautenbach 2003; May 2000). One study (Fridkin 2002 had medium microbial risk of bias and reported that two interventions that were each associated with statistically significant reduction in vancomycin use by 35% to 37% ( Table 1; Table 3) were associated with a statistically significant 13.2% difference in VRE between the intervention and control hospitals. The other studies had high microbial risk of bias and reported effects on vancomycin prescribing that had wide confidence intervals and were not statistically significant (Lautenbach 2003; Table 7; May 2000; Table 1). In particular the difference in VRE rates pre- and postintervention in Lautenbach 2003 was probably due to the study reporting only three pre-intervention data points with a steep increase in VRE, followed by levelling of VRE rates in the postintervention years. These data probably showed the natural history of emergence of VRE in this hospital rather than the effect of the modest (19.6%) reduction in vancomycin use in the postintervention phase.
Meta-analysis of persuasive versus restrictive interventions (52 studies, Figure 3)
de Man 2000, a cluster CCT, was the only study of a restrictive intervention that did not use an ITS design. Consequently this meta-analysis was confined to a meta-regression of ITS studies.
A total of 56 ITS studies were identified, of which 52 included data for the meta-analysis. The other four studies (Barlow 2007; Charbonneau 2006; Perez 2003; Suwangool 1991) used appropriate statistical models but did not include estimates of variance for the effect size at any of our time points, and these could not be recalculated from the raw data in the papers. The outcomes for the remaining 52 studies were prescribing (N = 38), microbial (N = 14) and cost (N = 4); four studies had more than one outcome.
Overall the studies showed a consistent impact on prescribing and microbial outcomes with at least 25% of studies showing an effect in the intended direction at each time point.
There were 23 studies of purely persuasive interventions: Abramowitz 1982; Adachi 1997; Ansari 2003; Avorn 1988; Berild 2002; Carling 2003; Dempsey 1995; Halm 2004; Hess 1990; Hulgan 2004; Kumana 2001; Lee 1995; Madaras-Kelly 2006; May 2000; McLaughlin 2005; Mol 2005; Patel 1989; Richardson 2000; Skaer 1993; Stevenson 1988; Van Kasteren 2005; Weinberg 2001; Wilson 1991.
There were 29 studies of restrictive interventions: Belliveau 1996; Bunz 1990; Bradley 1999; Calil 2001; Climo 1998; Everitt 1990; de Champs 1994; Gerding 1985; Gupta 1989; Himmelberg 1991; Huber 1982; Inaraja 1986; Khan 2003; Landman 1999; Lautenbach 2003; Leverstein 2001' McElnay 1995; McGowan 1976; McNulty 1997; Mercer 1999; Meyer 1993; Pear 1994; Richards 2003; Saizy-Callaert 2003; Salama 1996; Sirinavin 1998; Toltzis 1998; Woodward 1987; Young 1985.
Comparison 1: effect of restrictive versus persuasive interventions on prescribing outcomes
For prescribing outcomes the restrictive interventions had a statistically significantly greater effect at one month ( +32.0%, 27 studies, 95% confidence interval (CI) +2.5% to +61.4%), but at six months the difference had diminished to +10.1% (15 studies, 95% CI -47.5% to +66.0%), and at 12 or 24 months the persuasive interventions had greater effect, though none of the 6-, 12- or 24-month differences were statistically significant. Difference at 12 months was -24.6% (18 studies, 95% CI -71.9% to +22.6%) and difference at 24 months was -12.3% (11 studies, 95% CI -60.2% to +35.5%), Figure 3.
Comparison 2: effect of restrictive versus persuasive interventions on microbial outcomes
For microbial outcomes the restrictive interventions had a statistically significantly greater effect at 6 months ( +53.0%, 9 studies, 95% CI +30.6 to +75.4%), but at 12 months the difference had diminished to +16.2% (8 studies, 95% CI -21.9% to +54.4%) and at 24 months there was a small difference of -0.7% in favour of persuasive interventions (3 studies, 95% CI -49.1 to +47.8%, Figure 3).
For cost outcomes there were too few studies to compare effects.
Comparison 3: effect on clinical outcomes of interventions that aimed to increase effective antibiotic treatment (11 studies, Figures 4 and 5)
Three interventions used rapid reporting of microbiology results with increase in appropriate antibiotic therapy as the prescribing outcome measure (Bouza 2004; Bruins 2005; Doern 1994). Doern 1994 reported a significant reduction in mortality (Odds Ratio (OR) 0.53, 95% CI 0.32 to 0.90, P = 0.02), while the other two studies reported nonsignificant increases in mortality. The combined result was a risk ratio (RR) of 0.92 (95% CI 0.69 to 1.22, P = 0.56, Figure 4). All three studies also reported length of stay, but there was no significant difference between the intervention and control patients in any study.
|Figure 4. Forest plot of comparison: 1 Intended clinical outcomes, interventions intended to increase effective prescribing, outcome: 1.1 Mortality, interventions intended to increase appropriate antimicrobial therapy, all infections.|
Five interventions were intended to increase guideline compliance for pneumonia, three for community-acquired pneumonia (Chu 2003; Dean 2001; Dean 2006) and two for nursing home-acquired pneumonia (Dempsey 1995; Naughton 2001). Four studies reported mortality and all four interventions were associated with a reduction in mortality, of which two were statistically significant (Dean 2001; Dean 2006). The combined result was a RR of 0.89 (95% CI 0.82 to 0.97, P = 0.005, Figure 5). Dean 2006 also reported a significant reduction in readmissions. Four studies reported length of stay (Chu 2003; Dean 2001; Dean 2006; Dempsey 1995), but the format did not allow meta-analysis. Chu 2003 reported mean length of stay without standard deviation (SD), showing a decrease in both intervention and control hospitals but with no significant difference between them (P = 0.47). Dean 2001 reported that length of stay among post-guideline inpatients was similar to statewide trends (0.3 days shorter compared with pre-guideline, 95% CI 20.2 to 0.8 days; P = 0.21). Dean 2006 reported that in a logistic regression model, the OR for length of stay longer than seven days at intervention hospitals was 1.22 (95% CI 1.13 to 1.31; P = 0.001) compared with control hospitals. Length of stay longer than seven days decreased significantly between pre-implementation and postimplementation periods at intervention hospitals (OR 0.88, 95% CI 1.13 to 1.31 [this is what is reported in the paper but must be wrong]; P = 0.004). Dempsey 1995 reported that their intervention was associated with a significant reduction in length of stay, however length of stay decreased throughout both the control and intervention periods and our segmented regression analysis did not show any significant change in level (P = 0.74) or slope (P = 0.81).
|Figure 5. Forest plot of comparison: 1 Intended clinical outcomes, interventions intended to increase effective prescribing, outcome: 1.2 Mortality, interventions intended to increase antibiotic guideline compliance for pneumonia.|
Two studies showed that increased appropriate use of antibiotics for prophylaxis in surgery was associated with significantly reduced postoperative surgical site infections (Weinberg 2001; Zanetti 2003).
Burton 1991 showed that an increase in effective gentamicin serum concentrations was associated with significant reduction in length of stay. However, this study had a unit of analysis error so the confidence interval reported in the paper is too narrow. We did not include this study in any meta-analysis.
Comparison 4: effect on clinical outcomes of interventions intended to reduce excessive use of antimicrobials (14 studies, Figures 6-8)
In 14 studies clinical outcomes were used as a balancing measure, which is a term used in quality improvement to describe measures that address potential unintended consequences of changes to care processes (Lloyd 2004). In these studies the measures of clinical outcome were used to provide reassurance that reduction in what the authors had defined as excessive use of antibiotic prescribing was not associated with worse clinical outcomes.
Fourteen interventions that were intended to decrease antibiotic treatment reported clinical outcomes (Bailey 1997; Christ-Crain 2004; Christ-Crain 2006; de Man 2000; Fine 2003; Fraser 1997; Gums 1999; Micek 2004; Oosterheert 2005; Paul 2006; Singh 2000; Solomon 2001; Van Kasteren 2005; Walker 1998). However, one intervention was not associated with significant change in antibiotic prescribing (median duration of treatment 10 days in the intervention group versus nine days in the control group, the decreased duration as the intended effect (Oosterheert 2005)). We did not include this study in the meta-analyses.
Eleven interventions associated with decrease in excessive antibiotic prescribing reported mortality as an outcome (Bailey 1997; Christ-Crain 2004; Christ-Crain 2006; de Man 2000; Fine 2003; Fraser 1997; Gums 1999; Micek 2004; Paul 2006; Singh 2000; Solomon 2001). Two were intended to reduce the number of patients who received antibiotics for lower respiratory tract infections (Christ-Crain 2004; Christ-Crain 2006), three to reduce use of target antibiotics for empirical therapy (de Man 2000; Gums 1999; Paul 2006), two to reduce total duration of antibiotic therapy (Micek 2004; Singh 2000), three to reduce duration of IV antibiotics (Bailey 1997; Fine 2003; Solomon 2001) and one to reduce cost of antibiotics (Fraser 1997). No single intervention was associated with a significant increase in mortality and the combined result was a RR of 0.92 (95% CI 0.81 to 1.06, P = 0.25, Figure 6).
|Figure 6. Forest plot of comparison: 2 Clinical outcomes, interventions intended to decrease excessive prescribing, outcome: 2.1 Mortality, interventions intended to decrease excessive prescribing.|
Five interventions reported readmission as an outcome (Bailey 1997; Fine 2003; Fraser 1997; Solomon 2001; Walker 1998). Four were intended to reduce duration of intravenous antibiotics (Bailey 1997; Fine 2003; Solomon 2001; Walker 1998) and one to reduce the cost of antibiotics (Fraser 1997). Bailey 1997 was associated with a significant increase in total readmissions (RR 3.00, 95% CI 1.18 to 7.64) but there was no significant increase in infection-related readmissions (RR 1.33, 95% CI 0.31 to 5.66, P = 0.5). The combined result was a RR for total readmissions of 1.26 (95% CI 1.02 to 1.57, P = 0.03, Figure 7).
|Figure 7. Forest plot of comparison: 2 Clinical outcomes, interventions intended to decrease excessive prescribing, outcome: 2.2 Readmission, interventions intended to decrease excessive prescribing.|
Length of stay was reported by six studies in a format that allowed meta-analysis: (Christ-Crain 2004; Christ-Crain 2006; Gums 1999; Micek 2004; Paul 2006; Solomon 2001). The combined intervention effect was a reduction in length of stay by 0.04 days (95% CI -0.34 to +0.25, P = 0.78, Figure 8). In addition, Fine 2003 reported the median and interquartile range for length of stay with hazard ratio (HR). The intervention was not associated with a significant increase in HR for length of stay (1.16, 95% CI 0.97 to 1.38, P = 0.11).
|Figure 8. Forest plot of comparison: 2 Clinical outcomes, interventions intended to decrease excessive prescribing, outcome: 2.3 Lengh of stay, interventions intended to decrease excessive prescribing.|
One intervention that resulted in significant reduction in duration of surgical antibiotic prophylaxis was not associated with a significant change in postoperative wound infection (Van Kasteren 2005).
One study reported that substitution of ceftazidime with cefotaxime was associated with a significant increase in cefotaxime resistant Acinetobacter infections (Landman 1999; Table 11). There were no other examples of measurement of unintended microbial outcomes.
Impact of interventions on healthcare costs
See Table 13. Only 10 studies (11%) provided reliable data about both intervention costs and financial savings (Abramowitz 1982; Ansari 2003; Bailey 1997; Christ-Crain 2006; Gums 1999; Landgren 1988; Oosterheert 2005; Solomon 2001; Woodward 1987; Wyatt 1998). Other reports included statements such as the economic savings being "substantial in comparison to the modest costs" (Everitt 1990), or that modification of existing computer hardware or software incurred minimal costs (Zanetti 2003), without providing detail.
The limited information provided shows that intervention costs can be substantial. However, eight studies (Abramowitz 1982; Ansari 2003; Bailey 1997; Christ-Crain 2006; Gums 1999; Landgren 1988; Solomon 2001; Woodward 1987) reported that savings exceeded the cost of the intervention ( Table 13). The two exceptions were interventions that did not have a significant impact on antibiotic prescribing (Oosterheert 2005; Wyatt 1998).
The primary aim of this review was to identify interventions that are effective in promoting prudent antibiotic prescribing to hospital inpatients.
Summary of main results
There are many positive findings in this review: the 89 studies were conducted in 19 countries on five continents. They show that a variety of persuasive and restrictive interventions have changed antibiotic treatment for hospital inpatients and that changes in prescribing can be associated with improvement in outcomes. Specifically, the review now provides evidence that increase in effective treatment can be associated with reduced mortality and that decrease in excessive antibiotic use can be associated with improvement in microbial outcome without compromising clinical outcomes. This update to the review provides stronger evidence about clinical outcomes and now includes 11 interventions that aimed to decrease exposure to antibiotics by reducing the percentage of patients that received treatment (Christ-Crain 2004; Christ-Crain 2006; Franz 2004) or by shortening duration of treatment (Berild 2002; Fine 2003; Micek 2004; Oosterheert 2005; Senn 2004; Singh 2000) or prophylaxis (Landgren 1988; Van Kasteren 2005). External validity has also improved, with 15 studies in three or more hospitals and 9 in 10 or more hospitals. However, on the negative side, the 89 studies represent only approximately one-fifth of the published literature, which is still dominated by uncontrolled before-after studies or inadequate interrupted time series (ITS) or controlled before-after (CBA) studies that do not provide interpretable data (Ramsay 2003). Even between 2003 and 2006 only 49% of published studies met the minimum criteria of the Cochrane Effective Practice and Organisation of Care (EPOC) Group.
Overall completeness and applicability of evidence
Should interventions be persuasive or restrictive?
In the absence of direct comparisons any conclusions about the effectiveness of different interventions must be tentative. The problem of a lack of comparative studies is further compounded by the absence of standardization. In order to assess the sustained effect of any intervention we need data to assess change in level with the standard error (SE) for at least two time points. We suggest that for prescribing outcomes immediate effects should be assessed in the first six months, with sustained effects assessed at one year or longer. For microbial outcomes we suggest that immediate effects are assessed at six months with sustained effects assessed at one or two years. Our review suggests that restrictive interventions have a greater immediate impact than persuasive interventions. Previous EPOC reviews have not distinguished between these types of interventions and the frequent use of restrictive interventions may be peculiar to interventions relating to hospital prescribing. This finding is important because it supports restriction when the need is urgent (e.g. in an outbreak situation). However, this conclusion is based on indirect comparisons. The evidence base would be enormously enhanced by direct comparison, for example, by using time series analysis to measure the additional impact of a restrictive intervention added to that of a persuasive intervention. We also need more reassurance that restrictive interventions do not have unintended adverse clinical outcomes.
We considered further meta-analysis to see whether the addition of persuasive elements was associated with a more sustained intervention effect. We identified studies with data that allowed estimation of effect size at two or more time points. For microbial outcomes there is only one study in the review (McNulty 1997) that has a restrictive intervention with persuasive elements and effect size at both six and 12 months. Moreover there are only two studies in the review with data about microbial outcomes at 24 months postintervention (Carling 2003; Lautenbach 2003) and neither of these studies provides data about the immediate effect of the intervention. For prescribing outcomes effect size estimates at one and 12 months can be made for only one study of a purely restrictive intervention (Young 1985), and four studies of restrictive interventions with persuasive components (Belliveau 1996; Everitt 1990; McNulty 1997; Richards 2003).
Although there are not enough studies for meta-analysis of the effect of adding persuasive components to a restrictive intervention, there are two clear examples of multifaceted, restrictive interventions with diminishing effectiveness over time (Belliveau 1996; McNulty 1997). Hence the limited data show that the inclusion of persuasive components does not guarantee sustained effect for a restrictive intervention. The proportion of purely restrictive interventions has not changed much over time: 4 of 9 studies (44%) published up to 1990; 8 of 15 studies (53%) published from 1991 to 2000, and 3 of 8 studies (38%) published from 2001 to 2006. There may be enough studies to compare sustained effects of different intervention types in the next update.
Despite the limitation of indirect comparisons, restrictive interventions do seem to have a greater immediate impact than persuasive interventions. The intervention effects reported for restriction by removal ( Table 3) and for review and make change ( Table 8) were more consistent than for compulsory order forms ( Table 5) or expert approval ( Table 7). It is plausible that it is easier for prescribers to find a way around order forms and expert approval. Documented examples include misrepresenting clinical information (Calfee 2003; Linkin 2007) and delaying treatment to circumvent expert approval by an ID service that was off duty from 10pm (LaRosa 2007). Nonetheless, prescribers will find a way around any restriction, for example by going to other wards if antibiotics are removed from their clinical area or by changing a prescription back to the original. Consequently hospitals should not assume that restriction will work and must collect data to monitor impact. In addition to reducing the intended effect of restrictive interventions, misrepresentation of clinical information can have additional consequences. For example, misrepresenting infections as hospital-acquired in order to meet the criteria for use of restricted antibiotics has resulted in a pseudo-outbreak of hospital-acquired infection (Calfee 2003).
A major limitation of the evidence about restrictive interventions is that only one study provides data about clinical outcomes (de Man 2000). If hospitals do restrict the clinical freedom of their physicians then it is critical that they are not compromising the outcomes for their patients.
Social marketing and behaviour change theories
The most resource-intensive persuasive interventions used educational outreach, and these were not always effective ( Table 2). Two studies showed that academic detailing (Mol 2005) or review and recommend change (Bouza 2004) did not add significantly to the effect of simpler interventions (audit and feedback; Mol 2005, or reminders; Bouza 2004). Review and recommend change can be particularly resource-intensive because the system in some hospitals makes it difficult to identify and contact the doctor responsible for a specific prescription (Walker 1998). Consequently it is surprising that only one intervention in our review used a model for improvement based on involving the target professionals in setting priorities and in design and collection of measures for improvement (Weinberg 2001). In the quality improvement and patient safety literature there is growing evidence to support this type of intervention going back over a decade. In particular, successful interventions that are led by clinical teams may be easier to sustain and spread than interventions based on review and recommendation of change, which are inherently person-dependent (Nelson 1998). Recent systematic reviews have applied Control Theory (Gardner 2010; Michie 2009) or Feedback Intervention Theory (Hysong 2009) to meta-analysis, and have concluded that feedback is likely to be more effective if accompanied by action planning, helping participants to identify and overcome barriers to achieving their goals, which supports the model for improvement advocated by Nelson 1998.
There are several behavioural science theories which aim to explain why people behave in certain ways (Darnton 2008). These theories can be used in research to develop an understanding of the determinants of prescribing behaviours, in order to develop targeted interventions aiming to optimize prescribing. In public health, social marketing makes use of behavioural science theories and the principles of marketing to bring about change in health behaviours to reduce burden of disease in society. Social marketing at its core focuses on the target group to develop behaviour change interventions that are ‘customer oriented’, are based on theory, and are driven by primary research on what truly moves and motivates people (Morris 2009).Though the evidence on the application and utility of social marketing to change healthcare worker behaviours is limited, there is increasing evidence of use of some elements of social marketing contributing to interventions reported in antibiotic prescribing. Eight studies in this review could be classified as having elements of social marketing to investigate barriers to professional behaviour change as part of the intervention design (Barlow 2007; Dempsey 1995; Everitt 1990; Foy 2004; Mol 2005; Naughton 2001; Weinberg 2001; Wyatt 1998). However, none fulfilled the key additional element of explicit application of any behaviour change theory for the development of the interventions or the utilization of a defined strategy to market them. These results have been extended in a review of literature on social marketing applied to antibiotic stewardship published up to April 2011, which also found no evidence of the application of behavior change models (Charani 2011).
Three structural interventions focused on rapid reporting of laboratory results. While conventional methods for culture and susceptibility testing are time-consuming, two of these interventions (Doern 1994; Trenholme 1989) suggested that same-day result reporting may have significant benefits for antibiotic stewardship, including quicker administration of appropriate therapy and quicker streamlining.
Three structural interventions focused on the introduction of tests of inflammatory markers (Christ-Crain 2004; Christ-Crain 2006; Franz 2004), and all three showed that the use of these tests may significantly reduce the use of antibiotics for patients with low risk of infection ( Table 9). These are the only interventions in our review that reduced the number of patients who were treated with antibiotics in hospital, whereas rapid microbiology tests or polymerase chain reaction (PCR) tests for viruses had little impact on total antibiotic use (Bruins 2005; Doern 1994; Oosterheert 2005; Trenholme 1989). The evidence base for procalcitonin has recently been reviewed, and identified six additional studies that will be relevant to the next update of our review (Schuetz 2012).
Currently there is great emphasis on Point of Care Testing (POCT) that will allow informed antibiotic prescribing within one to two hours of presentation. In septic patients this could save lives (Kumar 2006) but there are many problems to overcome, not least expense. Risk assessment using an electronic decision support system may allow stratification of patients who would best benefit from such POCTs e.g. PCR of blood to increase detection of bacteraemia over conventional blood culture systems (Kofoed 2009), but this has yet to be tested in an intervention. Molecular POCTs are likely to be helpful in identifying specific organisms but identifying resistance profiles is more problematic; specific tests for vancomycin-resistant enterococci (VRE), methicillin-resistant Staphylococcus aureus (MRSA) and rifampin-resistant Mycobacterium tuberculosis are widely available, and those for some of the newer beta-lactamases such as New Delhi metallo-beta-lactamase 1 (NDM1) are a possibility. However these new technologies require careful assessment in well-designed intervention studies because the evidence that we have reviewed ( Table 9) shows that simply increasing the speed of reporting test results does not necessarily change prescribing behaviour.
How do changes in prescribing influence other outcomes?
The data show that interventions to change antibiotic prescribing were associated with decrease in Clostridium difficile ( Table 10), resistant gram-negative bacterial ( Table 11), MRSA and VRE ( Table 12). However, only six interventions (29%) provided reliable data about change in antibiotic prescribing, which is a major weakness in the evidence base because there are not enough data to estimate the likely impact of change in prescribing on microbial outcomes.
There has been a welcome increase in reporting clinical outcomes as a measure of unintended consequences of interventions that aim to reduce excessive prescribing. Failure to include measures of unintended consequences has been a long-standing problem with the use of performance data to change professional practice (Smith 1995). Limiting unintended consequences is an important goal of antimicrobial stewardship (McGowan 2012). However, the need for measures of unintended consequences is not specific to antimicrobial stewardship and extends beyond measures of clinical outcome. Recently 'Four Criteria for Accountability Measures That Address Processes of Care' have been proposed, of which one is 'Implementing the measure has little or no chance of inducing unintended adverse consequences' (Chassin 2010). The need for broader measures of unintended consequences is considered in more detail under construct validity in Quality of the evidence below.
In our review, all of the studies that included clinical outcomes as balancing measures were randomized controlled trials (RCTs) or cluster trials. In future information about balancing measures could be derived from routine data and included in ITS studies.
The most common measure of unintended clinical outcomes is mortality (Figure 6). Although it is reassuring to see no increase in total mortality associated with interventions that intend to reduce unnecessary antibiotic treatment, it would be preferable to develop indicators of mortality in patients with sepsis or defined infections. Five studies which included readmission as a balancing measure found that overall there was a significant increase in readmissions associated with the interventions (Figure 7). The study that reported the biggest change in total readmissions (Bailey 1997) also documented infection-related readmissions. These only accounted for 39% of readmissions within 30 days, and there was no significant difference between intervention and control groups for infection-related readmissions. It is unlikely that infection-related readmissions can be measured reliably from routine data (Davey 1995), which raises doubts about the validity of readmission as a balancing measure for interventions to reduce excessive antibiotic prescribing.
It is disappointing that still only 10 of 89 studies (11%) provided information about the costs of intervention, which is the same proportion as reported by a review of guideline implementation, in which only 25 of 235 reports (11%) described intervention costs (Grimshaw 2004). A survey of the resources available for guideline implementation in the UK concluded that most healthcare organizations do not have a budget that is adequate to support complex dissemination or implementation strategies. Instead they expect that their organizations will achieve change through dissemination of educational materials and short (lunchtime) educational meetings (Grimshaw 2004). Even the limited information about resources needed to implement interventions clearly shows that these are unrealistic expectations ( Table 13).
Quality of the evidence
We have considered three criteria for the included studies: internal validity, external validity and construct validity. Internal validity is concerned with problems such as bias or confounding in the study design. External validity is concerned with the extent to which results can be applied or generalized to people, settings or times other than those that were the subject of the study. Construct validity is concerned with the relationship between the study results and a theoretical construct of antibiotic stewardship (McGowan 2012).
The risk of bias in the studies that we have reviewed is variable, but there is a core of 49 studies (55%) with low or medium risk of bias or confounding. These show that a variety of persuasive and restrictive interventions do change antibiotic prescribing and that this can improve clinical or microbiological outcomes. A major gap in the evidence is that only six studies provide reliable data about change in antibiotic prescribing and microbial outcome.
The best evidence of external validity is provided by multicentre studies. In our review there are 15 studies that were done in three or more hospitals. Nine interventions aimed to decrease excessive antibiotic treatment (Charbonneau 2006; Fine 2003; Franz 2004; Fridkin 2002; Halm 2004; Landgren 1988; Paul 2006; Van Kasteren 2005; Wilson 1991) and included two cluster-RCTs (Fine 2003; Paul 2006). The remaining six studies were of interventions that aimed to increase effective antibiotic treatment (Chu 2003, Dean 2001; Dean 2006, Foy 2004, Naughton 2001, Wyatt 1998) and included two cluster-RCTs (Foy 2004; Wyatt 1998). Collectively these studies provide important evidence that interventions can work in multiple hospitals, both to decrease excessive prescribing (Charbonneau 2006; Franz 2004; Fridkin 2002; Landgren 1988; Paul 2006; Van Kasteren 2005) and to increase effective prescribing (Chu 2003; Dean 2001; Dean 2006).
Some evidence of external validity can be obtained by reproducing results from single hospitals in other hospitals but none of the single hospital studies is an exact reproduction of another study. However, we have been able to perform meta-regression of 52 ITS studies and meta-analysis of clinical outcomes, which is a major improvement in this update of the review.
The Holy Grail of implementation research is to provide health services with evidence about behaviour change that is similar to treatment trials, with robust estimates of effect size for well-defined groups of patients. Given the complexity of behaviour change strategies and healthcare organizations, it seems likely that local validation of interventions will always be required. Consequently hospitals will always have to evaluate their own interventions. We believe that the average hospital can aspire to low bias, high quality ITS evaluation of quality improvement interventions. These are data for improvement, not data for research. Nonetheless, improving the quality of ITS evaluations in single hospitals will lay the foundation for cluster-randomized trials with embedded time series (Brown 2006). Moreover, rigorous evaluation of interventions in single hospitals will help to set priorities for definitive research studies (Campbell 2007; MRC 2000).
Construct validity is involved whenever a test is to be interpreted as a measure of some attribute or quality which is not operationally defined (Cronbach 1955). There is general agreement that antibiotic stewardship has two competing objectives: first to ensure effective treatment of patients with infection, and second to minimize collateral damage from antibiotic use (Davey 2010; Dellit 2007; McGowan 2012). However, collateral damage to the normal human bacterial flora is an inevitable consequence of any antibiotic use. Consequently a successful intervention to increase necessary use of antibiotics will also increase collateral damage to the flora of the patients in the intervention. More importantly the intervention may unintentionally increase unnecessary antibiotic treatment for other patients. This has been documented in the USA where a performance measure that was designed to reduce delays in treatment for patients with pneumonia unintentionally increased unnecessary antibiotic treatment of patients who did not have pneumonia (Wachter 2008). Another example of unintended consequences was a pseudo-outbreak of hospital-acquired infection caused by doctors misdiagnosing patients in order to circumvent a restrictive antibiotic stewardship programme (Calfee 2003). However, this problem is not peculiar to antibiotic stewardship. The need to consider unintended consequences of changing care processes is a feature of any improvement project (Lloyd 2004; Randolph 2009). This problem can be addressed through balancing measures, which assess these potential unintended consequences and assure teams that they have indeed improved the overall system of care, rather than optimizing one part of the system at the expense of another (Randolph 2009). We are concerned that this issue is not addressed by the current Cochrane EPOC methods and that a recent review about audit and feedback does not mention adverse effects, balancing measures or unintended consequences (Ivers 2012).
Indirect evidence may already exist to support the construct of unnecessary antibiotic treatment. For example guidelines based on a systematic review of the literature have found no evidence to support giving antibiotic prophylaxis for surgery for more than 24 hours after the procedure (SIGN 2008). Consequently it may not be necessary to measure wound infection as an outcome of an intervention to increase the proportion of patients who receive prophylaxis for less than 24 hours (Landgren 1988). It is reassuring to have direct evidence to show that an intervention that successfully reduced duration of surgical prophylaxis was not associated with increased wound infection rates (Van Kasteren 2005). However, increasing the proportion of patients who discontinue antibiotic prophylaxis within 24 hours of surgery is one of a set of performance measures that addresses all four key criteria for accountability measures relating to processes of care (Chassin 2010). Hence we believe that it would not be necessary to measure wound infection rates in future interventions to improve this performance measure.
None of the 11 studies that aimed to increase effective antibiotic prescribing included information about unintended consequences. In contrast this update to the review does provide some important new evidence about two aspects of interventions to reduce excessive prescribing. First the evidence about lack of unintended consequences is stronger with fifteen studies and three meta-analyses ( Analysis 2.1; Analysis 2.2; Analysis 2.3). In particular there are now nine studies with data about mortality. Secondly, there are now three studies about reducing the percentage of patients who receive antibiotics, and eight studies about reducing the duration of antibiotic exposure without compromising clinical outcome. Nonetheless, more balancing measures of unintended consequences are required, especially the increase in resistance to antibiotics that are promoted in a policy change (Landman 1999; Meyer 1993).
In comparison with the 2005 review, this update comes closer to the aim of antibiotic stewardship because it provides more information about the safety of interventions to reduce excessive antibiotic prescribing and about the benefits of increasing effective prescribing,
CBA, CCT, RCT or ITS?
CCT or RCT designs were used in one or two hospitals in 22 studies. These designs provide very little protection against bias or confounding (Wagner 2002). Contamination from intervention to control arms is an important threat to the validity of RCTs conducted in a single hospital because of the rotation of junior staff. However because the majority of CCT or RCT studies in our review did not include baseline data, it is not possible to assess the degree of potential contamination. Even with baseline data, contamination is only one explanation for the observed improvement in the control groups. For example, Zanetti 2003 was conducted in a single hospital and showed marked improvement in both control and intervention groups. The authors suggested that contamination occurred and that it biased the results towards the null. However, a cluster-RCT performed in 25 hospitals (Wyatt 1998) also showed marked improvement in control and intervention arms, which is highly unlikely to have been due to contamination because of the study design. It is much more likely that the improvements in the control hospitals were due to increased awareness of the benefits of antibiotic prophylaxis in patients undergoing caesarean sections that was entirely independent of the intervention. An external secular trend can affect any study design but one of the key advantages of a cluster-randomized controlled trial is that it protects against contamination so that changes in the control group can be more reliably attributed to external secular trends. The only RCTs in fewer then three hospitals that had medium risk of bias were able to overcome the problems of allocation and contamination bias because the intervention was a laboratory test result that was only available for patients in the intervention arm (Christ-Crain 2004; Christ-Crain 2006) or by collecting baseline outcome data for two months before intervention to estimate the magnitude of possible observation bias (Senn 2004, Figure 3 in the original paper).
ITS represents a practical design for evaluating interventions in single hospitals that may provide better protection against bias and confounding than RCT and CBA designs (Wagner 2002). ITS studies have two features that are not present in CBA, RCT and CCT designs. Firstly, they provide information about pre-intervention trends and, secondly, they assess the extent to which the effect of an intervention is sustained. However, the information provided by studies would be enhanced enormously by using the same interval between points and by providing a minimum standard duration of pre- and postintervention phases. In this update, the meta-regression has been enhanced by calculation of effect sizes at 1, 6, 12 and 24 months. This allowed comparison of the immediate and sustained effects of restrictive versus persuasive interventions. However, this comparison would have been much stronger if more studies had provided data that allowed calculation of effect size at three or more time points. In future meta-analysis of time series data would be facilitated if all studies reported change in level with its standard error at 1, 6 and 12 months postintervention.
Implications for practice
A wide variety of interventions has been shown to be successful in changing antibiotic prescribing to hospital inpatients.Our meta-analysis provides evidence that restrictive interventions work faster than persuasive interventions, which supports the use of restrictive interventions when the need is urgent. However, we also found evidence that the effectiveness of some restrictive interventions diminishes over time so when restriction is justified it may be helpful to win hearts and minds through additional persuasive components. However, like other EPOC reviews we found that complex, multifaceted interventions were not necessarily more effective than simpler interventions. Review and recommend change was the most labour-intensive persuasive intervention but the effectiveness was not necessarily greater than for other, less intensive persuasive interventions. One of the most successful persuasive interventions (Weinberg 2001) involved the providers in the design of the intervention and in the measurement of intervention effect, which in many settings is likely to be more sustainable than review of individual patients by a professional from outside the provider team (Nelson 1998).
Implications for research
Greater external validity can be achieved by evaluating interventions in multiple hospitals, especially interventions that aim to reduce excessive antimicrobial treatment. Interrupted Time Series analysis is a valuable and practical method for evaluation of interventions in single hospitals. Standardizing methods for time series in single hospitals (for example, using monthly intervals, aiming for a minimum of one year of postintervention data and reporting intervention effects with standard error (SE) at 1, 6 and 12 months) would enhance the ability to compare results from single hospitals. Our new meta-regression method greatly enhanced comparison between studies and supports the use of restrictive interventions when the need is urgent. However, further meta-analysis will be enhanced by more standardized data.
We need more evidence about the effectiveness of interventions in a format that facilitates combining the results from several studies in order to provide robust estimates of effect size and assess the impact of effect modifiers. Combining results is likely to be particularly important in relation to clinical outcomes, studies from single hospitals usually being underpowered.
We found limited evidence from direct comparisons of the efficacies of different interventions, including simple versus multifaceted interventions. The ideal would be comparison by a cluster-randomized trial design, but such a design is expensive and must be directed towards high priority research questions. Multiphase time series data represents a more practical design format for generating reasonably robust data about the incremental impact of the components of multifaceted interventions (Wagner 2002), but this design was only used in one study (Mol 2005). In addition one RCT compared two levels of intervention with control (Bouza 2004).
The paucity of evidence about the cost effectiveness of guideline implementation in general is inexcusable and future studies should provide information about the resources required for development, dissemination and implementation of guidelines and other interventions (Grimshaw 2004).
It is strange that we have several examples of studies with clinical or microbiological outcomes that do not provide rigorous information about prescribing outcomes. There is some justification in a large multicentre study where mortality is the primary outcome measure (Dean 2001; Dean 2006), because measurement of prescribing outcomes would have added considerably to the cost of the study. However, in the majority of cases the problem was simply that the prescribing outcome data were described in terms of averages rather than as time series analyses, and correcting this would probably not have added significantly to the cost of the study.
Several of the studies that reported microbiological outcome data were unplanned interventions (Results Table 10; Table 11; Table 12). This is a serious risk of bias for any time series but is a particular problem with studies of infection because of the shape of the epidemic curve (Cooper 2003; Davey 2001).
Roger Finch, Giles Hartman and Eric Taylor were authors on the previous version of this review.
We are grateful to the British Society for Antimicrobial Chemotherapy (BSAC) for their significant financial support for the costs of meetings and statistical analysis.
Data and analyses
- Top of page
- Summary of findings [Explanations]
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Index terms
Appendix 1. EPOC Register Strategy 2009
Feb 2009. Reference Manager Software.
Terms were automatically truncated.
Search 1 OR Search 2 or Search 3 = 118 studies.
(TI,AB hospital OR hospitals OR inpatient OR inpatients OR intensive care OR emergency care OR emergency room OR triage OR trauma) AND (TIAB antibiotic OR antibiotics OR antimicrobial OR anti-bacterial)
(AB or TI Infection control) AND (AB antibiotic OR antibiotics OR antimicrobial OR anti-bacterial)
(AB methicill\* OR penicill\* OR ClarithromycinOR Tetracycline) AND (TIAB hospital OR hospitals OR inpatient OR inpatients OR intensive care OR emergency care OR emergency room OR triage OR trauma)
EPOC Register Strategy July 25,2007
Searched via Biblioscape Software)
(antibiotic* or antimicrobial*) all fields. Identified 94 studies.
Last assessed as up-to-date: 3 February 2009.
Protocol first published: Issue 1, 2002
Review first published: Issue 3, 2005
Contributions of authors
Erwin Brown (Medical Microbiologist): Chairman of Joint BSAC and Healthcare Infection Society (HIS) Working Party on Optimising Antibiotic Prescribing in Hospitals, initiated the review; designed and conducted the literature search; handsearched bibliographies of individual papers for additional references; reviewed all papers to identify those that reported the results of an intervention to change antibiotic prescribing; contributed to EPOC check sheets and data extraction.
Peter Davey (Clinical Pharmacologist): wrote the protocol; assisted with the literature search; reviewed all intervention studies for quality using EPOC methodology; re-analyzed data from included CBA, CCT and RCT studies; member of the writing group responsible for the first draft of the review and for final decisions about included studies; contributed to EPOC check sheets and data extraction.
Craig Ramsay (Statistician): re-analyzed all of the ITS studies that did not include regression methods in the original paper; member of the writing group responsible for the first draft of the review and for final decisions about included studies; contributed to EPOC check sheets and data extraction.
Phil Wiffen (Clinical Pharmacist, Director of Operation and Training at the UK Cochrane Centre): designed the Included Studies Table; advised on risk of bias; presentation of results; transferred review text, tables and figures to Review Manager 5; member of the writing group responsible for the first draft of the review and for final decisions about included studies; contributed to EPOC check sheets and data extraction.
Ian Gould (Microbiologist), Lynda Fenelon (Microbiologist), Alison Holmes (Hospital Epidemiologist) and Mark Wilcox (Microbiologist) are members of the BSAC/HIS Working Party; were involved in the design of the protocol; participated in the review of excluded and included studies; completed EPOC check sheets and extracted data from included studies; assessed microbial risk of bias; attended regular meetings of the Working Party and commented on the final draft of the review.
Esmita Charani (Pharmacist) participated in the review of social marketing study by adapting the EPOC definition of marketing, reviewing the relevant studies and writing additional text for the Results and Discussion sections.
Declarations of interest
Sources of support
- Aberdeen Royal Infirmary, Aberdeen, Scotland, UK.
- Emory University, Atlanta, Georgia, USA.
- Frenchay Hospital, Bristol, England, UK.
- Hackensack University Medical Centre, UK.
- Imperial College, London, England, UK.
- Leeds Royal Infirmary, Leeds, England, UK.
- St Vincent's University Hospital, Dublin, Ireland.
- Tel Hashomer Hospital, Tel Aviv, Israel.
- University of Dundee, Dundee, Scotland, UK.
- University of Nottingham, Nottingham, England, UK.
- Vale of Leven Hospital, Alexandria, Scotland, UK.
- UK Cochrane Centre, UK.
- British Society for Antimicrobial Chemotherapy, UK.
- Hospital Infection Society, UK.
Medical Subject Headings (MeSH)
*Drug Resistance, Bacterial; *Practice Patterns, Physicians'; Anti-Bacterial Agents [adverse effects; *therapeutic use]; Bacterial Infections [*drug therapy; prevention & control]; Cross Infection [*drug therapy; prevention & control]; Inpatients; Randomized Controlled Trials as Topic
MeSH check words
* Indicates the major publication for the study