Ebbing Lautenbach
Introduction
A sound understanding of the principles and approaches of epidemiology is critical to the study of infectious diseases in the healthcare setting. The urgency of comprehending and applying epidemiological principles is supported by the fact that the incidence and impact of healthcare-acquired infections (HAIs) and antimicrobial resistance have increased markedly since the last edition of this textbook. In addition, the applicability of techniques traditionally reserved for healthcare epidemiology have been recognized as uniquely suited to other emerging issues (e.g., patient safety, bioterrorism, drug use management, quality assessment, technology assessment, product evaluation, and risk management.) [1,2].
The value of epidemiological methods in the study of HAIs has been recognized for some time [3,4,5,6]. The ability to accurately quantify new patterns of HAIs, design and carry out rigorous studies to identify factors associated with disease, and devise and evaluate interventions to address emerging issues are vital to the study of HAIs. Indeed, during the past 5 years, there has been a renewed interest and vitality in efforts to explore previously unstudied aspects of epidemiological methods in the study of HAIs and antimicrobial resistance [7,8,9,10].
There are two primary goals of this chapter. The first goal is to review basic epidemiologic principles relevant to the study of HAIs including (1) measures of disease frequency, (2) study design, (3) measures of effect, (4) bias, and (5) confounding. The second goal is to discuss in more detail specific current epidemiologic issues in the study of HAIs including (1) quasi-experimental study design, (2) case-crossover study design, (3) control group selection in studies of antimicrobial resistance, (4) definitions of antibiotic exposure, and (5) assessment of mortality as an outcome of infection. The overriding focus of this chapter is discussion of epidemiologic methods applicable to the study of HAIs and antimicrobial resistance. The reader is also directed to numerous published textbooks solely dedicated to general epidemiology, infectious diseases epidemiology, and statistical analysis [11,12,13,14,15,16,17].
Measures of Disease Frequency
Accurately quantifying the frequency of disease is important for measuring the scope of the problem (i.e., how many
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people are affected by the disease) and for allowing comparison between different groups (i.e., those with and without a particular risk factor of interest). The most commonly used measures of disease frequency are prevalence and incidence.
Prevalence
Prevalence is defined as the proportion of people with disease at a given point in time (e.g., the proportion of hospitalized patients who have a HAI). This also may be referred to as the “point prevalence.”
Prevalence, which is a proportion and has no units, depends on both the incidence (i.e., the number of new episodes that develop) and the disease duration (i.e., how long a diseases lasts once it has developed). The greater the incidence and duration of disease, the higher the resultant prevalence. Prevalence is useful for measuring the burden of disease (i.e., the overall proportion of persons affected by the disease). Because all populations are dynamic, the prevalence may vary depending on when it is measured. If a dynamic population is at steady state (i.e., cases leaving = cases entering), the prevalence will be constant over time.
Incidence
Incidence is defined as the number of new episodes of diseases occurring in a specified period of time. Incidence may be described in several ways. Cumulative incidence is defined as the number of new episodes of disease in a particular time period divided by the total number of disease-free individuals at risk of the disease at the beginning of the time period (e.g., the proportion of patients who develop an HAI during hospitalization).
The cumulative incidence, like prevalence, is a proportion and thus has no units. To calculate the cumulative incidence, one must have complete follow-up on all individuals so as that their final disposition with regard to the outcome is known. Although this measure describes the total proportion of new episodes occurring in a time period, it does not describe when in the time period they occurred. For the cumulative incidence of HAIs, the period implied is the hospitalization until a first event or until discharge. However, patients do not stay in hospital and remain at risk for exactly the same period of time. Thus, comparing the cumulative incidence of infection among patient groups with differing lengths of stay may be very misleading.
The incidence rate (or incidence density) is defined as the number of new episodes of disease in a specified quantity of person-time of observation among individuals at risk (e.g., the number of HAIs per 1000 hospital days).
The value of this measure can be seen when comparing infection rates in groups that differ in their time at risk (e.g., short-stay patients vs. long-stay patients). When the time at risk in one group is much longer than in another, the incidence rate is the most convenient way to correct for time. This allows one to separate the effect of time (duration of exposure) from the effect of daily risk. Incidence rate usually is restricted to first events (e.g., the first episode of HAI). It is standard to consider only first events because second events are not statistically independent from first events in the same individuals.
Unlike cumulative incidence, the incidence rate does not assume complete follow-up of subjects. However, even when follow-up is complete (and thus cumulative incidence could be calculated), reporting the incidence rate may still be preferable. Cumulative incidence reports only the overall number of new episodes occurring during the period (regardless of whether they occur early or late in the time period). By comparison, the incidence rate, by incorporating the time at risk, accounts for potential difference in time to occurrence of the event.
The assumption in the incidence rate is that all time at risk is equal (e.g., the likelihood of developing a HAI in the first 3 days after hospital admission is the same as the likelihood of developing an infection during days 4 through 6 of hospitalization). If all time periods are not equivalent, the incidence rate may be misleading.
Study Design
Various study designs may be chosen when seeking to address a clinical question. These study designs, in order of increasing methodological rigor, include case report, case series, ecologic study, cross-sectional study, case-control study, cohort study, and randomized controlled trial. Randomized controlled trials, case-control studies, and cohort studies are considered analytic studies while the other designs are considered descriptive studies.
Case Report/Case Series
A case report is the clinical description of a single patient (e.g., a single episode of a patient with a bloodstream infection due to fluoroquinolone-resistant Escherichia coli (FQREC)). A case series is a report of >1 patient with the disease of interest. In addition to serving as a clinical or therapeutic example, a case report/series can function to generate hypotheses that may then be tested
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in future analytic studies. The primary limitation of a case report/series is that it describes at most a few patients and may not be generalizable. In addition, because a case report/series does not include a comparison group, one cannot determine which characteristics in the description of the patient(s) are unique to the illness.
Ecologic Study
In an ecologic study, one compares geographic and/or time trends of an illness to trends in risk factors (i.e., a comparison of annual hospital-wide use of fluoroquinolones (FQs) with annual prevalence of FQREC). Ecologic studies often use aggregate data that are routinely collected for other purposes (e.g., antimicrobial susceptibility patterns from a hospital's clinical microbiology laboratory). As a result, one advantage of the ecologic study is that it is often relatively quick and easy to do. Thus, such a study may provide early support for or against a hypothesis. However, one cannot distinguish between various hypotheses that might be consistent with the data. Perhaps most important, ecologic studies do not incorporate patient-level data. With such a study, one knows only that there is a correlation between annual hospital-wide use of FQs and yearly prevalence of FQREC, not that the actual patients infected with FQREC received FQs.
Cross-Sectional Study
A cross-sectional study assesses the status of subjects with regard to the risk factor and disease at the same point in time. A cross-sectional study to investigate FQREC might assess all patients currently hospitalized and whether they have an FQREC infection and whether they are receiving FQs. A cross-sectional study is relatively easy to carry out because all subjects are assessed at only one point in time. As such, this type of study may provide early evidence for or against a hypothesis. A major disadvantage of a cross-sectional study is that it does not capture the concept of elapsed time (i.e., it is not possible to determine whether the risk factor or the outcome came first). Furthermore, a cross-sectional study does not provide information about the transition between health states.
Case-Control Study
To compare the various types of analytic studies (e.g., case-control, cohort, experimental-randomized controlled trial), it is useful to consider the traditional 2 by 2 table (Figure 8-1). While all three study designs seek to investigate the association between a risk factor (or exposure) and an outcome of interest, they differ fundamentally in how patients are enrolled in the study. In a case-control study, patients are entered into the study based on the presence or absence of the outcome (or disease) of interest. These two groups (i.e., those with the disease and those without the disease) are then compared to determine if they differ with regard to their presence of risk factors of interest.
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Figure 8-1 Study designs. |
A case-control study design, which is always retrospective, is particularly attractive when the outcome being studied is rare because one may enroll all patients with the outcome of interest. As such, this study design is much more efficient than the comparable cohort study in which a group of patients with and without an exposure of interest would need to be followed for a period of time to determine who develops the outcome of interest. Another advantage of the case-control study is that one may study a number of risk factors for the outcome of interest. One limitation of a case-control study is that only one outcome may be studied. Another disadvantage of this approach is that one cannot directly calculate the incidence or relative risk because the investigator fixes the number of cases and controls to be studied.
Of great importance in a case-control study is the process by which cases and controls are selected. Cases may be restricted to any group of diseased individuals. However, they must arise from a theoretical source population so that a diseased person not selected is presumed to have arisen from a different source population. For example, in studying risk factors for nosocomial FQREC infection, the theoretical source population could be considered to be the population of patients hospitalized at the institution. Thus, a patient at that institution with a clinical FQREC isolate would be included as a case. However, a patient with FQREC infection at a different hospital would not be included. Cases also must be chosen in a manner independent of their status with regard to an exposure of interest.
Careful attention also is required when selecting controls. Controls should be representative of the theoretical source population that gave rise to the cases. Thus, if a control were to have developed the disease of interest, the person would have been selected as a case. In the preceding example, controls may be randomly selected from among all non-FQREC infected patients in the hospital.
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In investigating the possible association between prior FQ use and FQREC infection, these two groups (i.e., patients with FQREC infection and a random sample of all other hospitalized patients) could be compared to determine what proportion of patients in each group had experienced recent FQ exposure. Finally, like cases, controls must be chosen in a manner independent of their status with regard to an exposure of interest and should not be selected because they have characteristics similar to cases. The selection of controls in case-control studies of antimicrobial resistance will be discussed in more detail in a later section of this chapter.
Cohort Study
Unlike a case-control study, patients are entered into a cohort study based on the presence or absence of an exposure (or risk factor) of interest (Figure 8-1). These two groups (i.e., those with the exposure and those without the exposure) are then compared to determine whether they differ with regard to the development of the outcome of interest. A cohort study may be either prospective or retrospective, which depends on when it is conducted with regard to when the outcome of interest occurs. If patients are identified as exposed or unexposed and then followed forward in time to determine whether they develop the outcome, it is a prospective cohort study. If the study is conducted after all outcomes have already occurred, it is a retrospective cohort study. As an example, one might identify all patients who receive a FQ in the hospital (i.e., the exposed) and compare them to a randomly selected group of patients who do not receive a FQ (i.e., the unexposed). These groups could then be followed forward to determine what proportion of patients in each group develops the outcome of interest (i.e., FQREC infection).
An advantage of a cohort study is that one may study multiple outcomes from a single risk factor or exposure. Also, this study design allows the investigator to calculate an incidence and a relative risk in comparing the two groups. Potential limitations of a cohort study include substantial time and cost requirements due to often prolonged follow-up of subjects. In addition, if the outcome is rare, a large number of subjects will need to be followed to ensure adequate sample size. Finally, the longer the study duration, the more likely subjects will be lost to follow-up, potentially biasing the study results. Some of these limitations are mitigated in a retrospective cohort study because outcomes already have occurred and patients do not need to be followed prospectively.
Randomized Controlled Trial
The randomized controlled trial is very similar to the cohort study (Figure 8-1). However, in a cohort study, patients are enrolled already with or without the exposure of interest. In a randomized controlled trial, the investigator assigns the exposure randomly. This study design provides the most convincing demonstration of causality because patients in both groups should (provided randomization has worked appropriately) be equal with regard to all important variables except the one variable (exposure) manipulated by the investigator. While randomized controlled trials may provide the strongest support for or against an association of interest, they are costly studies, and there may be ethical issues that preclude their conduct. For example, in studying the association between FQ use and FQREC infection, one could not ethically assign patients to receive FQ if they did not require the drug. One alternative to the randomized controlled trial is the quasi-experimental study design, which will be discussed in a later section of this chapter.
Measures of Effect
Relative Risk (RR)
The RR (also called the risk ratio) is the ratio of two probabilities: the probability of the outcome among the exposed divided by the probability of the outcome in the unexposed (Figure 8-2). An RR can be calculated from a cohort study or a randomized controlled trial because from these study designs, one can derive population-based rates or proportions. An RR of 1.0 is called the value of no effect, or the null value. An RR = 2.0 means that the exposed subjects were twice as likely to have the outcome of interest as the unexposed subjects. An RR = 0.5 means that the exposed were half as likely to experience the outcome as the unexposed, indicating a protective effect of the exposure.
Odds Ratio (OR)
In a case-control study, subjects are enrolled based on the outcome of interest. One then compares these two groups (i.e., those with the outcome and those without it) to determine what proportion of subjects in each group demonstrates a risk factor of interest. Unlike the cohort study, one cannot directly calculate an RR. What one can calculate in a case-control study is the OR, which is defined as the odds of exposure in subjects with the outcome divided by the odds of exposure in subjects without the outcome (Figure 8-2). An OR = 1.0 is called the value of no effect, or the null value.
As noted, one cannot calculate an RR from a case-control study because this type of study offers no insights into the absolute rates or proportions of disease among subjects. However, in situations in which the disease under study is rare (<10%), the OR derived from a case-control study closely approximates the RR that would have been derived from the comparable cohort study. Figure 8-2 shows how the case-control formula approaches the formula for RR when the rare outcome criterion is met.
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Figure 8-2 Relative risk and odds ratio. |
Measures of Strength of Association
p Value
The chi-square test for comparison of two binomial proportions is the most common method of measuring strength of association in a 2 by 2 table. This calculation is identical for all 2 by 2 tables whether or not data were derived from a cohort or case-control study. When the chi-square value has been calculated, the associated probability that the observed difference between binomial proportions could have arisen by chance alone can be looked up. A p value of <.05 indicates that an effect at least as extreme as that observed in the study is unlikely to have occurred by chance alone because there is truly no relationship between the exposure and the disease. Although this is the conventional interpretation, there is nothing particularly unique about the 0.05 cutoff for statistical significance. One limitation of the p value is that this value reflects both the magnitude of the difference between the groups and the sample size. Consequently, even a small difference between groups (if the sample size is large) may be statistically significant even if it is not clinically important. Conversely, a larger effect that would be clinically important may not be statistically significant if the sample size is small.
95% Confidence Interval
Because of the limitations of the p value just noted, it is preferable to report the 95% confidence interval (CI) for a given RR or OR. The 95% CI provides a range within which the true magnitude of the effect (i.e., the RR or the OR) lies with a certain degree of assurance. Observing whether the 95% CI crosses 1.0 (i.e., the value of null effect) provides the same information as the p value. If the 95% CI crosses 1.0, the p value will almost never be <0.05. The impact of the sample size can be ascertained from the width of the confidence interval. The narrower the confidence interval, the less variability was present in the estimate of the effect, reflecting a larger sample size. The wider the confidence interval, the smaller the sample size. When interpreting results that are not statistically significant, the width of the confidence interval may be helpful. A narrow confidence interval implies that there is most likely no real effect whereas a wide interval suggests the data also are compatible with a true effect and that the sample size was simply inadequate.
Bias
Bias is the systematic error in the collection or interpretation of data. Types of bias include information bias (i.e., distortion in the estimate of effect due to measurement error or misclassification of subjects on one or more variables) and selection bias (i.e., distortion in the estimate of effect resulting from the manner in which subjects are selected for the study). For example, a common type of information bias in case-control studies is recall bias. One may compare patients with a FQREC infection to a random sample of noninfected controls in an effort to identify risk factors for FQREC infection. If patients with a FQREC infection are aware of their diagnosis, they may be more likely to try to identify possible reasons for experiencing a resistant infection. If this group is more likely to remember recent antibiotic use than are controls, the association between recent antibiotic use and FQREC infection will be spuriously strengthened.
The potential for bias must be addressed when the study is designed because it cannot be corrected during the analysis of the study. Indeed, blinding in randomized controlled trials is a commonly used method to minimize the potential for bias in such studies. In addition to evaluating whether bias may exist, one also must consider the likely impact of the bias on the study results. Bias may be nondifferential (i.e., biasing toward the null hypothesis and making the two groups being compared look artificially similar) or differential (i.e., biasing away from the null hypothesis and making the two groups being compared look artificially dissimilar).
Confounding
Confounding occurs when the association observed between an exposure and outcome is due, in part, to the effect
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of some other variable. To be a confounder, a variable must be associated with both the exposure and outcome of interest but cannot be a result of the exposure. Confounding can result in an over- or underestimate of the effect of the exposure of interest. For example, in assessing the association between an FQREC infection and mortality, one must consider underlying severity of illness as a potential confounder. Patients with more severe illness are more likely to develop FQREC infection. In addition, more severe illness also is more likely to result in mortality. Thus, because it is associated with both the exposure and outcome of interest, severity of illness is a potential confounding variable. Unlike bias, a confounding variable may be controlled for in the study analysis. However, to do this, data regarding the presence or absence of the confounder must be collected during the study. Thus, it also is important to consider the potential for confounding variables in the design of the study.
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TABLE 8-1 |
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Special Issues in Healthcare Epidemiology Methods Quasi-Experimental Study Design
In addition to the study designs reviewed previously, the quasi-experimental study is a design frequently employed in healthcare epidemiology investigations [18]. This design also is frequently referred to as a “before-after” or “pre-post intervention” study [19,20]. The goal of a quasi-experimental study is typically to evaluate an intervention without using randomization. The most basic type of quasi-experimental study involves the collection of baseline data, the implementation of an intervention, and the collection of the same data following the intervention. For example, the baseline prevalence of FQREC in a hospital would be calculated, an intervention to improve FQ use would then be instituted, and the prevalence of FQREC again would be measured after a prespecified time period. Many different variations of quasi-experimental studies exist and include (1) institution of multiple pretests (i.e., collection of baseline data on more than one occasion), (2) repeated interventions (i.e., instituting and removing the intervention sequentially), and (3) inclusion of a control group (i.e., a group on which baseline and subsequent data are collected but on which no intervention is implemented) (Table 8-1) [18,21].
Although often employed in evaluations of HAI interventions, critical evaluation of the advantages and disadvantages of quasi-experimental studies has only recently been conducted [18,21]. Indeed, a recent systematic review of four infectious diseases journals found that during a two-year period, 73 articles focusing on infection control and/or antimicrobial resistance used a quasi-experimental study design [18]. Of these articles, only 12 (16%) used a control group, 3 (4%) provided justification for the use of the quasi-experimental study design, and 17 (23%) mentioned at least one of the potential limitations of such a design [18]. More attention has recently been focused on increasing the quality of quasi-experimental study design and conduct to enhance the validity of conclusions
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drawn regarding effectiveness of interventions in the areas of infection control and antibiotic resistance [18].
The quasi-experimental study design offers several advantages. The study designs available when one wishes to study the impact of an intervention are limited. In general, a well-designed and adequately powered randomized controlled trial provides the strongest evidence for or against the efficacy of an intervention. However, there are several reasons why a randomized controlled trial may not be feasible in the study of infection control interventions. Randomizing individual patients to an intervention of infection control interventions often is not a reasonable approach given the person-to-person transmission of resistant pathogens. One might consider randomizing specific units or floors within one institution to receive the intervention. However, these units are not self-contained, and patients and healthcare workers frequently move from unit to unit. Thus, any effect on reduced transmission/acquisition of new resistant infections noted in the intervention units is also likely to result in some reduction in resistant infections in nonintervention areas (i.e., contamination). This would bias the results toward the null hypothesis (i.e., no effect of the intervention). Similarly, if only certain areas in an institution were randomized to the intervention, enhanced attention to infection control that might be part of an intervention would likely be evident to nonintervention floors, given that many healthcare workers (e.g., physicians, nurses) work in multiple areas. This might result in enhanced infection control practices on nonintervention floors, which would bias the results toward the null. In such a situation, a well-designed quasi-experimental study offers a compelling alternative approach. In addition, this study design is frequently used when it is not ethical to conduct a randomized controlled trial. In addition, when an intervention must be instituted rapidly in response to an emerging issue (e.g., an outbreak), the first priority is to address and resolve the issue. In this instance, it would be unethical to randomize an intervention across patient groups.
Several primary limitations exist in quasi-experimental studies including regression to the mean, uncontrolled confounding, and maturation effects. Implementation of an intervention is often triggered in response to a rise in the rate above the norm [22]. The principle of regression to the mean predicts that these elevated rates will tend to decline even without intervention. This may serve to bias the results of a quasi-experimental study because it may be falsely concluded that an effect is due to the intervention [19,20]. Several approaches may be employed to address this potential limitation. First, incorporating a prolonged baseline period before the intervention permits an evaluation of the natural fluctuation in rates of the outcome over time and permits a more comprehensive assessment of possible regression to the mean. Second, changes in the outcome of interest may be measured at a control site (e.g., another institution) during the same time period. Finally, the use of segmented regression analysis may assist in addressing possible regression to the mean in that the immediate change in prevalence coincident with the intervention will be assessed as will the change in slope over time [23,24,25].
Uncontrolled confounding, another potential limitation in quasi-experimental studies, is most likely to occur when variables other than the intervention change over time or differ when comparing the pre- and postintervention periods [19,20]. This limitation can be addressed by measuring known confounders (e.g., hospital census, number of admissions) and controlling for them in analyses. However, not all confounders are known or easily measured (e.g., quality of medical and nursing care). To address this, one may assess a nonequivalent dependent variable to evaluate the possibility that factors other than the intervention influenced the outcome [18,21]. A nonequivalent dependent variable should have similar potential causal and confounding variables as the primary dependent variable except for the effect of the intervention. For example, in assessing the impact of an intervention to limit FQ use on FQREC prevalence, one might consider incidence of catheter-associated bloodstream infections as a nonequivalent dependent variable. While FQREC prevalence and catheter-associated bloodstream infection might both be affected by such factors as patient census, it is unlikely that FQ use specifically would affect the incidence of catheter-associated bloodstream infections.
Maturation effects are related to natural changes that patients experience with the passage of time [19,20]. In addition, cyclical trends (e.g., seasonal variation) may be a threat to the validity of attributing an observed outcome to an intervention. This potential limitation may be addressed through approaches noted earlier including the assessment of a prolonged baseline period, use of control sites, implementiation of interventions at different time periods at different sites, and assessment of a nonequivalent dependent variable.
Case-Crossover Study Design
The case-crossover study design also has been increasingly recognized as a useful approach when addressing issues in healthcare epidemiology [26]. In this design, each case serves as her or his own control (i.e., self-matching). For each subject, the exposure status is measured in the “case” time period occurring shortly before the outcome. Then this is compared to the exposure status in one or more earlier “control” time periods. Then, RR are estimated by comparing the frequency of exposure immediately before the case event (the case period) vs. the earlier period (the control period).
This study design offers several advantages. Because cases serve as their own controls, the design adjusts for many of the differences between cases and controls that might
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confound a traditional case-control study. This study design also is less susceptible to confounding by indication [27]. All retrospective studies relying on patient recollection of exposure data may suffer from recall bias. Another potential advantage of the case-crossover study is that the same person is recalling data from both the control and case time periods since because person serves as his or her own control [27,28].
Several disadvantages of the case-crossover design also exist. An underlying assumption in this design is that confounders are not changing over time in a systematic way; otherwise, this may be a source of confounding [27]. In addition, bias could result from temporal changes in the exposure of interest or through the selection of the control time window [27].
The case-crossover study design is ideally suited to studying brief exposures with immediate and transient effect and acute outcomes with abrupt onset (e.g., motor vehicle accidents, injury) [29,30]. Also, exposures must vary over time within an individual; otherwise, there would be no ability to compare exposed and unexposed periods within the individual. However, it has been suggested that with lengthened exposure assessment windows for both the case and control time periods, case-crossover methods also may be useful for studying exposures with prolonged effects and outcomes with insidious onsets [31,32,33]. This may be particularly relevant for studying the adverse effects of prolonged drug exposures (e.g., antimicrobials) given the concerns regarding control selection bias and confounding inherent in traditional case-control studies of adverse effects [31].
With regard to healthcare epidemiology specifically, this design has been used successfully to study sharps injuries in healthcare workers [28]. In this study, the case-crossover design was well suited to assess the relationship between brief, transient exposures, such as fatigue or rushing, and the acute event of a sharps injury. Another recent study used a case-crossover approach to study the association between wet, humid weather and the incidence of legionellosis [34]. This approach was useful in controlling for seasonal factors that might confound the relationship between weather and disease occurrence to facilitate the identification of acute weather patterns associated with legionella infection [34].
Control Group Selection in Studies of Antimicrobial Resistance
Many studies have focused on identifying risk factors for antimicrobial resistance. The majority of these studies have been case-control–designed studies. As noted previously, how controls are selected in case-control studies is critical in ensuring the validity of study results. Recent work has highlighted this issue of control group selection specifically for studies of antibiotic resistance [7,35,36,37,38].
Historically, two types of control groups have been used in studies of antimicrobial resistant organisms [7]. The first type of control group is selected from patients who do not harbor the resistant pathogen. The second type of control group is selected from among subjects with a susceptible form of the infection. For example, in a study of risk factors for infection with FQREC in hospitalized patients, the first type of control group would be selected from among the general hospitalized patient population while the second control group would be selected from among those patients with a FQ-susceptible E. coli (FQSEC) infection. The choice of control group should be based primarily on the clinical question being asked. While use of this second type of control group has historically been a more common approach, it has recently been demonstrated that the use of this type of control group (e.g., patients infected with the susceptible form of the organism) may result in an overestimate of the association between antimicrobial exposure and resistant infection [37,38]. Using the example of FQREC, the explanation for this finding has been postulated as follows: If the controls are represented by patients with FQSEC infections, it is very unlikely that these patients would have recently received FQs (i.e., the risk factor of interest) because exposure to FQs may have eradicated FQSEC colonization. Thus, the association between FQ use and FQREC would be overestimated [39]. A limitation of using the first type of approach (i.e., using patients without infection as controls), is that, in addition to identifying risk factors for resistance, this approach also identifies risk factors for infection with that organism in general (regardless of whether the infection is resistant or susceptible). Thus, there is no way to distinguish the degree to which a risk factor is associated with the resistance phenotype vs. associate with infecting organism in general [36].
One concern with using the second type of control group (i.e., selecting from all hospitalized patients) is the potential for misclassification bias. Specifically, subjects selected as controls who have never had a clinical culture obtained may in fact harbor unrecognized colonization with the resistant organism under study [35]. Because it is probable that patients colonized with the resistant organism would likely have had greater prior antimicrobial exposure than subjects not colonized, this misclassification would likely result in a bias toward the null (i.e., the cases and controls would appear falsely similar with regard to prior antimicrobial use). Another concern with using the second type of control group and identifying patients who have never had a clinical culture as controls is that differences between cases and controls may reflect the fact that clinical cultures were performed for case-patients but not for controls. Because procurement of cultures is not a random process but is based on clinical characteristics, it is possible that the severity of illness or antibiotic exposure may be greater among cases regardless of the presence of antibiotic-resistant infection [7]. One potential approach would be to limit eligible controls to those patients for whom at least one clinical culture has been performed
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and does not reveal the resistant organism of interest. Such a negative culture would suggest that the patient is likely not colonized with the resistant organism. However, recent work has demonstrated that using clinical cultures to identify eligible controls leads to the selection of a control group with a higher co-morbidity score and greater exposure to antibiotics compared with a control group for which clinical cultures were not performed [35].
One proposed approach to addressing the difficulties in control group selection in studies of antimicrobial resistance is the case-case-control study design [36,40,41,42]. In this design, two case-control studies effectively are performed. In the first study, cases are defined as those patients harboring the resistant organism while controls are those patients without the pathogen of interest. In the second study, cases are instead defined as those patients harboring the susceptible bacteria while controls, similar to those in the first approach, are those patients without the pathogen of interest [36]. These two separate studies are then carried out with risk factors from the two studies compared qualitatively. This approach allows for the comparison of risk factors identified from the two studies to indicate the relative contribution of the resistant infection over and above simply having the susceptible infection. A potential limitation in this approach is the difficulty in matching for potential confounders because of the use of only one control group [36]. Because there are two different case groups, case variables (e.g., duration of hospitalization, patient location) cannot be used for matching. In addition, the qualitative comparison of results from the two studies in this design leaves open the question as to how much of a difference in results is meaningful.
Definitions of Antibiotic Exposure
Many studies have sought to uncover risk factors for infection or colonization with resistant organisms [10,43]. Elucidating such risk factors is essential to inform interventions designed to curb further emergence of resistance. Past studies have particularly focused on antimicrobial use as a risk factor because it can be modified in the clinical setting [44,45]. However, the approaches used to define prior antibiotic exposure vary considerably across studies [7]. More important, only recently have attempts been made to identify the impact of differences in these approaches on study conclusions.
A recent study investigated methods used in past studies to describe the extent of prior antibiotic use (e.g., exposure yes/no vs. duration of exposure) and the impact of using different methods on study conclusions [46]. A systematic review of all studies investigating risk factors for extended-spectrum β-lactamase-producing E. coli and Klebsiella species (ESBL-EK) was conducted. Among the 25 included studies, prior antibiotic use was defined as a categorical variable in 18 studies, four studies defined prior antibiotic exposure as a continuous variable, and three studies included both a categorical and a continuous variable to describe prior antibiotic exposure. Only one paper provided an explicit justification for its choice of variable to describe prior antibiotic exposure. The authors then re-analyzed a dataset from a prior ESBL-EK risk factor study [47], developing two separate multivariable models, one in which prior antibiotic use was described as a categorical variable (e.g., exposure yes/no) and one in which antibiotic use was described as a continuous variable (e.g., antibiotic days). Results of the two multivariable models using different methodological approaches differed substantially. Specifically, third-generation cephalosporin use was a risk factor for ESBL-EK when antibiotic use was described as a continuous variable but not when antibiotic use was described as a categorical variable [46].
These results suggest that describing prior antibiotic use as a categorical variable may mask significant associations between prior antibiotic use and resistance. For example, when the categorical variable is used, a subject who received only one day of an antibiotic would be considered identical to a subject who received 30 days of the same antibiotic. However, the risk of resistance is almost certainly not the same in these two individuals. Describing prior antibiotic use as a continuous variable allows for a more detailed characterization of the association between length of exposure and resistance. Recent work in the medical statistics literature emphasizes that the use of cutpoints can result in misinterpretation of data and that dichotomizing continuous variables reduces analytic power and makes it impossible to detect nonlinear relationships [48]. Indeed, the relationship between prior antimicrobial use and resistance may not be linear (i.e., the risk of resistance may not increase at a constant rate with increasing antimicrobial exposure). It is possible that the risk of resistance does not increase substantially until a certain amount of antimicrobial exposure has been attained (e.g., a “lower threshold”). A more precise characterization of this “lower threshold” would serve to better inform antibiotic use strategies.
Another issue regarding defining prior antimicrobial use centers around how specific agents are grouped. For example, antibiotic use could be classified by agent (e.g., cefazolin), class (e.g., cephalosporins), or spectrum of activity (e.g., gram-negative). Antibiotics are frequently grouped together in classes even though individual agents within the class may differ significantly [49], and such categorizations may mask important associations. It is unknown whether using different categorization schemes results in different conclusions regarding the association between antibiotic use and resistance. A recent study explored these issues, focusing on ESBL-EK as a model [50]. In a systematic review, 20 studies of risk factors for ESBL-EK that met inclusion criteria revealed tremendous variability in how prior antibiotic use was categorized. Categorization of prior antibiotic use was defined in terms of the specific agents, drug class, and often a combination of both. No
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study justified its choice of categorization method. There also was marked variability across studies with regard to which specific antibiotics or antibiotic classes were assessed. As expected, a majority of the studies (n=16) specifically investigated the use of β-lactam antibiotics as risk factors for ESBL-EK. A variable number of studies also examined the association between the use of other antibiotics and ESBL-EK infection: aminoglycosides (9 studies), FQs (10 studies), and trimethoprim-sulfamethoxazole (7 studies). In a reanalysis of data from a prior study of risk factors for ESBL-EK [47], two separate multivariable models of risk factors for ESBL-EK were constructed, one with prior antibiotic use categorized by class and the other with prior antibiotic use categorized by spectrum of activity [50]. The results of these multivariable models differed substantially. Recent work has reported similar findings when focusing on risk factors for carbapenem-resistant Pseudomonas aeruingosa [51].
Another final important issue is how remote antibiotic use is assessed. A recent systematic review of studies investigating risk factors for ESBL-EK (noted earlier) [46] found that the time window during which antibiotic use was reviewed ranged from 48 hours to one year before the resistant infection. Furthermore, studies often did not explicitly state how far back in time prior antibiotic use was assessed [46].
Assessment of Mortality as an Outcome of Infection
Studies have increasingly focused on more clearly identifying the impact of HAIs and antimicrobial resistance [52]. These studies seek to identify risk factors for negative outcomes such as mortality, increased cost, and prolonged length of hospital stay. Increasing attention has recently been paid to potential methodological issues in assessing the relationship between an antimicrobial-resistant infection and mortality [7,52]. One important issue is the need to control for severity of illness. An oft-noted risk factor for resistant infection is greater underlying severity of illness. However, severity of illness also is a predictor of mortality. These characteristics suggest that severity of illness is likely to be an important confounder in the association between resistant infection and mortality (i.e., severity of illness is associated with both the exposure and outcome of interest). Several measures assess severity of illness including the Acute Physiology and Chronic Health Evaluation (APACHE) II score [53], and the McCabe-Jackson Score [54]. It is important to note that no severity of illness score has been developed or validated specifically to predict outcome in patients with infection. Regardless of the measure used, it is critical to assess the score and control for it in studies assessing the impact of resistant infection on mortality.
It is important to carefully consider when severity of illness is assessed [55]. The vast majority of studies have assessed severity of illness at the time the infection is diagnosed (i.e., when the culture is initially drawn). However, the culture is generally obtained because of clinical suspicion of infection, suggesting that infection has already progressed at some time point before the culture was obtained. Because infection will typically also lead to a more severe illness, it is likely that severity of illness measured on the day the culture is obtained is more accurately an intermediate variable (e.g., infection leads to a more severe illness, which then ultimately leads to death). Controlling for an intermediate variable in this way usually causes an underestimate of the effect of the exposure of interest on the outcome [56]. To avoid this issue, it has been suggested that severity of illness be assessed at least 48 hours before the date the culture was obtained to provide a more reasonable assessment of the patient's underlying severity of illness rather than the severity of illness caused by the infection itself [55]. Interpreting the results of studies that control for severity of illness on the day the culture is obtained should be interpreted with caution because they may represent an underestimate of the true association between resistant infection and mortality [55].
Length of stay in the hospital before infection also is an important potential confounder in the association between resistance and mortality. Increased length of stay is a risk factor for resistant infection and is a risk factor for negative clinical outcomes [7]. A recent study assessing mortality associated with E. coli bacteremia first compared patients with E. colibacteremia to unmatched controls without bacteremia and then compared them to patients without E. coli bacteremia but matched by prior length of hospital stay [57]. The authors found similar associations between E. coli bacteremia and mortality regardless of whether matching was used [57]. Although these results suggest little impact of controlling (through matching) for length of stay, the results should be interpreted with caution because the prior length of stay in the patient groups was relatively short (median 6 days) [7].
Similar to the preceding discussion, the choice of control group also is relevant in studies of outcomes [55]. Of note, because studies addressing outcomes related to infection are primarily cohort studies, “controls” in these studies are more appropriately referred to as the “unexposed” or “reference” group. As in case-control studies of antibiotic resistance, there are effectively two choices for a reference group. In the first, patients with a resistant infection (e.g., FQREC) are compared with patients with the susceptible counterpart (e.g., FQSEC). In the second type of control group, patients with a resistant infection (e.g., FQREC) are compared to patients with no infection. Although either approach is valid, each addresses slightly different clinical questions. In the first, the result provides an assessment of the added impact of harboring a resistant infection vs. a susceptible infection. In the second, the impact of having a resistant infection vs. no infection is ascertained. It has been demonstrated that the latter type of comparison typically
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results in a higher estimate of the impact of resistance on mortality [58,59].
A final issue with regard to assessment of mortality as an outcome is how mortality is defined. Crude in-hospital mortality has been the most common measure of mortality likely because it is the least subjective in its assessment. However, this definition of mortality fails to distinguish those patients in which infection clearly resulted in death as opposed to those in which infection occurred but was likely unrelated to mortality (e.g., infection occurs several weeks before death). Some studies have proposed approaches to categorizing the outcome of mortality relative to how likely it is to have been a result of infection. One approach would be to assign an arbitrary time period after the infection (e.g., one week) beyond which the occurrence of mortality would be assumed to be independent of the infection. Another approach has proposed categories designed to assess attributable mortalityas an outcome [47,60,61,62]. In this definition, the possible outcomes are classified as follows: (1) mortality directly attributable to infection: death during hospitalization in the setting of clinical evidence of active infection and a positive culture result, (2) mortality indirectly attributable to infection: failure or further compromise of an organ system due to infection and death occurring during hospitalization as a result of organ failure, (3) mortality unrelated to infection: death occurring during hospitalization after an episode of infection but due to causes independent of the infectious process, and (4) survival: patient discharged alive from the hospital. The proportion of deaths directly and indirectly attributable to infection define the attributable mortality. While this approach may more appropriately designate mortality as attributable to infection, many of the criteria remain quite subjective. Of note, recent studies using both this approach and crude in-hospital mortality as outcomes found no substantive differences in final study results [63,64].
Summary
To best respond to the increasingly complicated field of HAIs and antimicrobial resistance, a strong understanding of epidemiologic principles and approaches is essential. This chapter has reviewed basic principles of epidemiology and a number of more specific topics with particular relevance to HAIs and antimicrobial resistance. While a resurgence in the study of epidemiological methodology in HAIs has occurred in recent years, this field of inquiry must continue to expand in the future. Only by providing the most rigorously derived evidence can we hope to devise and implement successful strategies to limit future infections in the healthcare setting.
References
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