Standard versus biofilm antimicrobial susceptibility testing to guide antibiotic therapy in cystic fibrosis
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To compare biofilm antimicrobial susceptibility testing‐driven therapy to conventional antimicrobial susceptibility testing‐driven therapy in the treatment of P. aeruginosa infection in people with CF.
Background
Description of the condition
Cystic fibrosis (CF) is the most common life‐limiting genetic disorder in the Caucasian population. Respiratory failure secondary to chronic bacterial respiratory infection is the leading cause of death in CF (Gibson 2003). One of the most important bacteria that infect the airways of CF patients is Pseudomonas aeruginosa (P. aeruginosa) (Burns 2001; Henry 1992; Kosorok 2001; Pamukcu 1995). The more aggressive use of antibiotic therapy to treat these infections is considered to be an important factor for the improved survival seen in people with CF (Frederiksen 1996; Ramsey 1996). The antibiotics used to treat pulmonary infections in CF are typically chosen based on the results of antimicrobial susceptibility testing done in the laboratory (Waters 2008). Although the length of antibiotic treatment may vary, acute pulmonary exacerbations are typically treated with intravenous antibiotics for 14 days.
Description of the intervention
In the laboratory, bacteria are cultured from respiratory tract specimens obtained from people with CF. The bacteria are then traditionally grown in a planktonic mode of growth and exposed to fixed concentrations of different antibiotics (Jorgensen 2009). The potential efficacy of antibiotics is then determined by measuring their ability to inhibit the growth of these bacteria. Each bacterium is then reported to be susceptible, intermediate or resistant to each tested antibiotic. Clinicians would subsequently choose antibiotics, to which the bacterium is susceptible, to treat their patients. This type of conventional antimicrobial susceptibility testing based on planktonic growth of bacteria has been validated in the treatment of urinary tract and blood stream infections, in which susceptibility results correlate well with clinical outcomes (MacGowan 2008). This is not the case for the treatment of pulmonary infections in CF (Gilligan 2006). Studies have shown that there is not any association between conventional antimicrobial susceptibility results and clinical outcomes, in terms of lung function, following the administration of antibiotics for a pulmonary exacerbation (Smith 2003). In addition, susceptibility testing is typically done on one colony selected from a similar appearing growth of an organism (morphotype). However, different colonies from the same morphotype of P. aeruginosa grown from a CF sputum sample, for example, may have different antimicrobial susceptibility results, making it difficult to evaluate the role of conventional susceptibility testing in CF (Foweraker 2005).
In fact, there is considerable in vitro and in vivo evidence to suggest that P. aeruginosa actually grows in a biofilm (or slime layer) in the airways of CF patients with chronic pulmonary infections (Murray 2007; Drenkard 2002; Singh 2000). Biofilms are communities of bacteria embedded in an exopolysaccharide matrix (coating of sugar molecules) that make them more resistant to antimicrobial killing (Prince 2002). In the laboratory, bacteria are usually grown as a biofilm by growing them on plastic pegs (Ceri 1999). In order to perform biofilm antimicrobial susceptibility testing, the bacteria are then exposed to antibiotics by placing the plastic pegs into wells (usually in a 96‐well plate) containing different antibiotics at fixed concentrations. The ability of the antibiotic to inhibit or kill the bacteria in a biofilm can be determined by a variety of methods. There are limitations to this system however. In contrast to this assay (or test) that grows P. aeruginosa on plastic pegs, studies have shown that P. aeruginosa actually forms a biofilm within the mucous itself (Bjarnsholt 2009). In addition, in this assay, P. aeruginosa is grown under aerobic conditions but there is considerable evidence that organisms grow within an anerobic environment in the CF lung (Tielen 2010).
Biofilm antimicrobial susceptibility testing has generally been done in research settings. There is, however, a commercially available biofilm antimicrobial susceptibility panel, called BioFILM PA TM (Innovotech Inc), which is licensed by Health Canada for antimicrobial susceptibility testing of P. aeruginosa.
How the intervention might work
It would thus seem logical to reason that antimicrobial susceptibilities determined for bacteria growing as a biofilm, rather than planktonically, would lead to more reliable antibiotic choices in treating P. aeruginosa in the CF airway. Previous use of biofilm susceptibility assays for isolates of P. aeruginosa from patients with CF have shown that antimicrobial susceptibilities based on biofilm growth differ significantly from those based on planktonic growth. In one study, biofilm inhibitory concentrations (concentrations of antibiotics that inhibit biofilm growth) for P. aeruginosa were much higher than the corresponding conventionally determined minimum inhibitory concentrations (MICs) for several classes of antibiotics including ß‐lactams (Moskowitz 2004), leading to different simulated antibiotic regimens (Moskowitz 2005). Using a similar biofilm antimicrobial susceptibility assay, the Calgary Biofilm Device, minimal biofilm eradication concentrations of selected antibiotics were found to be 100 to 1,000 times the MICs for certain organisms including P. aeruginosa (Ceri 1999). Hence, antibiotic susceptibilities based on biofilm‐grown P. aeruginosa may lead to different antibiotic choices with potentially improved microbiological and clinical outcomes.
Why it is important to do this review
Antibiotic therapy plays an important part in maintaining the health and longevity of patients with CF. However, there is currently no way of choosing antibiotic therapy in CF that is known to result in improved clinical outcomes. Conventional antimicrobial susceptibility testing may not accurately reflect how bacteria grow in the CF lung; biofilm antimicrobial susceptibility testing may be a better methodology, leading to improved clinical outcomes and less adverse effects. To answer this question, this review will compare biofilm antimicrobial susceptibility testing‐driven therapy to conventional antimicrobial susceptibility testing‐driven therapy in the treatment of P. aeruginosa infection in people with CF.
Objectives
To compare biofilm antimicrobial susceptibility testing‐driven therapy to conventional antimicrobial susceptibility testing‐driven therapy in the treatment of P. aeruginosa infection in people with CF.
Methods
Criteria for considering studies for this review
Types of studies
Randomized controlled trials (RCTs).
Types of participants
Adults and children (with all levels of disease severity) diagnosed with CF, confirmed with sweat test or genetic testing (or both), who have P. aeruginosa isolated from respiratory specimens. Respiratory tract specimens will include sputum, throat swabs or bronchoalveolar lavage specimens.
Types of interventions
Biofilm antimicrobial susceptibility testing‐driven therapy compared to conventional antimicrobial susceptibility testing‐driven therapy in the treatment of P. aeruginosa infection in people with CF. Therapy will include single or multiple antibiotics, oral, inhaled or intravenous antibiotics.
Types of outcome measures
Primary outcomes
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Lung function
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forced expiratory volume at one second (FEV1) (absolute values (litres or per cent (%) predicted or both))
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forced vital capacity (FVC) (absolute values (litres or % predicted or both))
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mid‐expiratory flow (FEF25‐75) (absolute values (litres or % predicted or both))
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Pulmonary exacerbations, defined as an increase in respiratory symptoms requiring antibiotic therapy (Fuchs 1994)
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number of pulmonary exacerbations
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time between pulmonary exacerbations
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time to subsequent exacerbation
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Adverse events (including numbers of events, proportion of patients withdrawing and proportion of patients changing therapy)
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mild: transient event, no treatment change e.g. rash
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moderate: treatment discontinued e.g. nephrotoxicity
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severe: causing hospitalization or death
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Secondary outcomes
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Sputum bacterial density (measured in colony forming units/ml (CFU/ml))
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Quality of life (QOL) (as measured by a validated QOL score i.e. CFQoL (Gee 2000), CFQ‐R (Quittner 2009))
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Mortality
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Nutritional parameters
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weight
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height
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body mass index (BMI)
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Number of hospitalizations
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Use of oral antibiotics
Search methods for identification of studies
Electronic searches
We will identify relevant trials from the Group's Cystic Fibrosis Trials Register.
The Cystic Fibrosis Trials Register is compiled from electronic searches of the Cochrane Central Register of Controlled Trials (Clinical Trials) (updated each new issue of The Cochrane Library), quarterly searches of MEDLINE, a search of EMBASE to 1995 and the prospective handsearching of two journals ‐ Pediatric Pulmonology and the Journal of Cystic Fibrosis. Unpublished work is identified by searching the abstract books of three major cystic fibrosis conferences: the International Cystic Fibrosis Conference; the European Cystic Fibrosis Conference and the North American Cystic Fibrosis Conference. For full details of all searching activities for the register, please see the relevant sections of the Cystic Fibrosis and Genetic Disorders Group Module.
We will also check the National Institutes of Health (NIH) sponsored website www.clinicaltrials.gov for any ongoing studies with potential interim results.
Searching other resources
We will check the reference lists of all trials identified for any further relevant trials. We will also contact biotech companies that are involved with biofilm antimicrobial susceptibility technology for any additional information.
Data collection and analysis
Selection of studies
The two authors (VW, FR) will independently apply the inclusion criteria to all potential trials. The authors will not be blinded to the trials. If a disagreement occurs, they will resolve it by discussion with a third person (Nikki Jahnke (NJ)).
Data extraction and management
Using a data collection form, the two authors (VW, FR) will independently obtain data from published reports or from trialists. If a disagreement occurs, they will resolve it by discussion with a third person (NJ). In addition to information about study references and authors and verification of study eligibility, the data collection form will include information about the methods of the study (e.g. study duration, type of trial, blinding, number of dropouts and potential confounders). The authors will also report characteristics of the study participants including age, sex and setting of the study on the form. Furthermore, they will also describe the intervention with regards to type of antibiotic, route of delivery, doses and length of treatment. The authors will collect data for all randomised participants. When possible the authors will collect the following data: the mean change (before and after antibiotic therapy) in FEV1 and FVC, FEF 25‐75; the mean hospital length of stay; the time to subsequent pulmonary exacerbation; the number of adverse events; the mean QOL score after antibiotic therapy; the mean change in sputum bacterial density (before and after antibiotic therapy); the number of mortalities and change in weight (before and after antibiotic therapy). For each mean value, the authors will also obtain the standard deviation (SD) (variation from the average). For time to next exacerbation, they will collect log‐rank estimates (popular method of comparing the survival of groups, which takes the whole follow up period into account) and Cox model estimates (also known as proportional hazards model: a statistical model that asserts that the effect of the study factors (e.g. the intervention of interest) on the hazard rate (the risk of occurrence of an event, such as death, at a point in time) in the study population is multiplicative and does not change over time).
We plan to measure outcomes at less than a week, one to two weeks, more than two weeks to three weeks, more than three weeks to four weeks and at monthly intervals, if applicable. The outcome 'Time to next pulmonary exacerbation' will be measured in monthly intervals after these time points. We will also consider outcomes measured at other time points.
Assessment of risk of bias in included studies
The authors will assess the included studies for the following types of bias: selection bias (bias in choosing study participants); performance bias (bias in the care of study participants); attrition bias (bias in how participants who are lost to follow up are handled); detection bias (biased assessment of outcome); and reporting bias (bias in the reporting of study outcomes) using the following strategies as outlined below (Higgins 2011a).
Assessment of generation of allocation sequences
We will assess each trial as to the generation of allocation sequences:
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Low risk of bias: if allocation sequence is suitable to prevent selection bias (i.e. random numbers table, drawing envelopes, tossing a coin, throwing dice etc);
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High risk of bias: if allocation sequence could be related to prognosis and thus introduce selection bias (i.e. assigning participants based on case record number, date of birth, date of admission etc);
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Unclear risk of bias: if the trial is described as randomised but the method used to generate the allocation sequence is not stated.
Assessment of concealment of allocation sequences
We will also assess the method used to conceal the allocation sequences in each trial:
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Low risk of bias: if participants and investigators cannot predict which group the participant will be assigned to (i.e. coded drug containers, central randomisation, numbered, sealed, opaque envelopes etc);
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High risk of bias: if participants and investigators can predict which group the participant will be assigned to and thus introduce selection bias (i.e. open allocation schedule, non‐opaque envelopes etc);
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Unclear risk of bias: if the method of concealing the allocation sequence is not described.
Assessment of blinding
In order to determine the potential for performance and detection bias, we will assess each trial with respect to the degree of blinding:
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the participant is blinded to participant assignment;
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the care provider is blinded to participant assignment;
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the investigator measuring study outcomes is blinded to participant assignment.
There will be a high risk of bias if there is no blinding with respect to one or more of the above categories. There will be a low risk of bias if the trial is blinded to all three. There will be an unclear risk of bias if the trial does not specify the degree of blinding in each of the three categories.
Incomplete outcome data
To assess for the possibility of attrition bias, we will examine each trial with respect to:
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whether or not it was stated how many participants were lost to follow‐up and why they were lost to follow‐up;
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whether or not an intention‐to‐treat analysis was used (i.e. inclusion in the final analysis of all randomised participants into a trial in the groups to which they were randomised irrespective of what happened subsequently).
There will be a high risk of bias if an intention‐to‐treat analysis was not used. There will be a low risk of bias if the number and reason for loss of follow‐up is specified and if an intention‐to‐treat analysis was used. There will be an unclear risk of bias if the trial does not specify the above outlined information.
Assessment of selective reporting
We will review the included studies for selective reporting (Higgins 2011a). We will compare the original trial protocols with the published paper(s) to ensure all planned outcomes are reported. If the original trial protocols are not available, we will review the 'Methods' and 'Results' sections and the authors will use their discretion to determine if selective reporting has occurred.
Assessment of other potential sources of bias
We will also review the included trials for other potential sources of bias that will threaten the validity of the study. These will include: early cessation of the trial; if the interim results affect the study conduct; deviation from the study protocol; inappropriate administration of a co‐intervention; contamination; the use of an insensitive instrument to measure outcomes; selective reporting of subgroups; fraud; inappropriate influence of funding agencies and industry sponsorship; null bias due to the interventions being poorly delivered; or the existence of a pre‐randomization of an intervention that could affect the effects of the randomized intervention (Higgins 2011a).
Incorporating assessments of study validity in reviews
We plan to weigh studies according to their assessed validity by using the inverse of the variance for the estimated measure of effect. If we consider there was a high risk of bias, we will investigate the effects of this with a sensitivity analysis (see below).
Measures of treatment effect
For dichotomous data, we will gather information on participants randomised to each treatment group, based on an intention‐to‐treat analysis, and the number of events. We plan to include interim results from individual randomised participants from ongoing studies in the analysis. We will define time points for each study outcome according to when it was measured (less than a week, one to two weeks, more than two weeks to three weeks, more than three weeks to four weeks and at monthly intervals). We will analyse study outcomes separately according to these time points. We plan to pool the treatment effect across studies to determine a risk ratio (RR) and its 95% confidence intervals (CIs) for each study outcome.
For continuous data, we will calculate the difference between the mean (average) values (MD) of treatment effect for each group. As a summary statistic across trials, we will use the MD if the same scale is used, or the standardised mean difference (SMD) if different scales are used (e.g. QOL measurements) both with 95% CIs. For time‐to‐event data, most studies use Kaplan‐Meier survival analysis. We will thus collect log‐rank estimates and Cox model estimates to subsequently summarize the time‐to‐event data as a hazard ratio (HR) with 95% CIs (Higgins 2011b; Parmar 1998).
Unit of analysis issues
We will include data from cluster‐randomized trials if the information is available. For cluster‐randomized trials, the intracluster correlation coefficient (ICC) will be calculated according to Donner (Donner 2001). We will also include data from cross‐over trials if the information is available. Continuous data from cross‐over trials will be analyzed using one of three approaches: treat the study as a parallel trial and pool the interventional periods and compare these to the pooled placebo periods; including data from the first period only and approximating a paired analysis; by imputing missing SDs (Higgins 2011c). Cross‐over trials with dichotomous outcomes require more complicated methods and we will consult with a statistician as recommended (Elbourne 2002).
Dealing with missing data
Data are often missing for participants who are lost to follow‐up (whether or not trialists collect data on all outcomes). We will perform an available‐case analysis (analysing data for every participant for whom the outcome is available) in these situations. We will report the percentages of participants from whom no outcome data were available on the data collection form. We will include data on only those whose results are known, using as a denominator the total number of people who completed the trial for the particular outcome in question. We will consider variation in the degree of missing data across studies as a potential source of heterogeneity.
Assessment of heterogeneity
In performing a meta‐analysis, we will measure the variability of results between trials (heterogeneity) using the chi‐squared test (where a P value of less than 0.10 indicates the presence of heterogeneity) (Higgins 2011d) and the I2 method outlined by Higgins (Higgins 2003). The I2 statistic describes the percentage of total variation across studies that is due to heterogeneity rather than by chance. It is calculated using Cochran's heterogeneity statistic and the degrees of freedom. The I2 statistic can range from 0% to 100%. A value of 0% indicates no observed heterogeneity and larger values show increasing heterogeneity. A value greater than 50% may be considered substantial heterogeneity.
Assessment of reporting biases
To investigate whether our review is subject to publication bias, we will construct a funnel plot, if we include sufficient trials (at least 10). In the absence of bias, the plot should resemble a symmetrical inverted funnel (Higgins 2011d). If there is asymmetry, we will consider publication bias and other reasons (such as location biases, true heterogeneity, poor methodological quality of smaller studies etc.) as a potential cause.
Data synthesis
If the trials are considered clinically similar (e.g.: pulmonary exacerbation studies with different types of antibiotics, oral versus intravenous, different lengths of treatment) enough to combine, we will investigate statistical heterogeneity as outlined below. If there is no significant heterogeneity, we will calculate the pooled effect estimates using a fixed‐effect model. If we identify heterogeneity, we will perform a random‐effects meta‐analysis to address heterogeneity among trials.
Subgroup analysis and investigation of heterogeneity
If we find substantial heterogeneity as defined above (Higgins 2003), we will explore the potential causes of this (i.e. different types of antimicrobial treatment such as oral, inhaled or intravenous; different participant populations etc.) and if possible, conduct subgroup analyses of the trials. For example, trial results may vary if different types of antibiotic treatments are used (e.g. oral, inhaled or intravenous) for the treatment of pulmonary infection in different settings, e.g. acute pulmonary exacerbation or as suppressive treatment. In addition, results may vary if one study has more adult participants that can produce sputum (a more accurate sample with potentially more reliable culture results) and another trial has more pediatric participants where only throat swabs are used (a less reliable respiratory tract sample). Finally, there may be differences depending on whether antibiotics are used to treat a first time infection (eradication) versus an established, chronic infection (over 50% of cultures positive in previous 12 months).
Sensitivity analysis
If we are able to include at least 10 studies in the review, we will perform a sensitivity analysis to determine whether the conclusions are robust to decisions made during the review process such as the inclusion or exclusion of particular trials from a meta‐analysis, imputing missing data or choice of a method for analysis. We will investigate whether changing which trials are included, based on our assessment of the risk of bias (including or excluding trials with any high risk of bias) or changing our chosen statistical model (i.e. random‐effects model compared to a fixed‐effect model) changes the results of our review. If the sensitivity analysis does not significantly change the results, it strengthens the confidence that can be placed in these results. We will present the results in an influence plot, as appropriate.
