Epidemiologic Methods for Investigating Infections in the Healthcare Setting
Jennifer H. Han
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-associated 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 has 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 now (3,4,5,6). The ability to accurately quantify new patterns of HAIs, design and carry out rigorous studies to identify the factors associated with disease, and devise and evaluate interventions to address emerging issues are vital to the study of HAIs. Indeed, during the past decade, 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 (3,4,5,6,7).
There are two primary goals of this chapter. The first goal is to review the basic epidemiologic principles relevant to the study of HAIs, including (a) measures of disease frequency, (b) study design, (c) measures of effect, (d) bias, and (e) confounding. The second goal is to discuss in more detail specific current epidemiologic issues in the study of HAIs, including (a) quasi-experimental study design, (b) case-crossover study design, (c) control group selection in studies of antimicrobial resistance, (d) definitions of antibiotic exposure, and (e) 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, or statistical analysis (8,9,10,11,12,13,14).
MEASURES OF DISEASE FREQUENCY
Accurately quantifying the frequency of disease is important for measuring the scope of the problem (i.e., how many 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 an HAI). This may also 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 disease 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 are equal to cases entering), the prevalence will be constant over time. Surveillance systems in Western European countries have more commonly measured the prevalence rather than the incidence of HAIs at the country and hospital levels (see Chapter 6).
INCIDENCE
Incidence is defined as the number of new episodes of disease 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 a complete follow-up on all individuals so 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 beginning of hospitalization until a first event or until discharge. However, patients do not stay in the hospital and remain at risk for exactly the same period of time. Thus, comparing the cumulative incidence of HAI among patient groups with differing lengths of stay may be very misleading.
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 beginning of hospitalization until a first event or until discharge. However, patients do not stay in the hospital and remain at risk for exactly the same period of time. Thus, comparing the cumulative incidence of HAI 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 1,000 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 is usually 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 a complete follow-up of subjects. However, even when the 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 an HAI in the first 3 days after hospital admission is the same as the likelihood of developing an infection during days four through six of hospitalization). If all time periods are not equivalent, the incidence rate may be misleading. The Centers for Disease Control and Prevention’s (CDC’s) National Healthcare Safety Network (NHSN) predominantly uses incidence rate calculations rather than prevalence rates (see Chapter 5).
STUDY DESIGN
Various study designs may be chosen when seeking to address a clinical question. These study designs, in order of increasing methodologic 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 as analytic studies, whereas the other designs are considered as 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 more than one 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 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. Thus, these data may be true but unrelated.
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 × 2 table (Figure 9.1). 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 on the basis of 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.
determine if they differ with regard to their presence of risk factors of interest.
 Figure 9.1. Study designs. (Adapted from Lautenbach E. Epidemiological methods in infection control. In: Lautenbach E, Woeltje K, eds. Practical Handbook for Healthcare Epidemiologists. Thorofare, NJ: Slack; 2004:65.) |
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 the cases and controls are selected. The 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 healthcare-associated FQREC infection, the theoretical source population could be considered to be the population of patients hospitalized at the institution who did not have community-acquired FQREC infections at the time of admission. Thus, a patient at that institution with a clinical FQREC isolate recovered after admission would be included as a case. However, a patient with FQREC infection at a different hospital would not be included. The cases also must be chosen in a manner independent of their status with regard to an exposure of interest.
Careful attention is also required when selecting the controls. The 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, the controls may be randomly selected from among all non-FQREC-infected patients in the hospital. 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 the 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 on the basis of the presence or absence of an exposure (or risk factor) of interest (Figure 9.1). 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 the 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 the patients who receive an FQ in the hospital (i.e., the exposed) and compare them to a randomly selected group of patients who do not receive an 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 HAI).
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 an 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 an adequate sample size. Finally, the longer the study duration, the more likely the subjects will be lost to follow-up, potentially biasing the study results. Some of these limitations are mitigated in a retrospective cohort study because the outcomes have already occurred and the patients do not need to be followed prospectively.
RANDOMIZED CONTROLLED TRIAL
The randomized controlled trial is very similar to the cohort study (Figure 9.1). 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, if well designed, provides the most convincing demonstration of causality because the 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 HAI, 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 relative risk (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 9.2). 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 of 2.0 means that the exposed subjects were twice as likely to have the outcome of interest as the unexposed subjects. An RR of 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 on the basis of 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 9.2). An OR of 1.0 is called the value of no effect, or the null value.
 Figure 9.2. Relative risk and odds ratio. (Adapted from Lautenbach E. Epidemiological methods in infection control. In: Lautenbach E, Woeltje K, eds. Practical Handbook for Healthcare Epidemiologists. Thorofare, NJ: Slack; 2004:65.) |
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 the 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 9.2 shows how the case-control formula approaches the formula for RR when the rare-outcome criterion is met.
MEASURES OF STRENGTH OF ASSOCIATION
P Value
The chi-square test for comparison of two binomial proportions is the most common method of measuring the strength of association in a 2 × 2 table. This calculation is identical for all 2 × 2 tables whether or not the 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 it 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 <.05. The impact of the sample size can be ascertained from the width of the CI. The narrower the CI, the less variability present in the estimate of the effect, reflecting a larger sample size. The wider the CI, the smaller the sample size. When interpreting results that are not statistically significant, the width of the CI may be helpful. A narrow CI implies that there is most likely no real effect, whereas a wide interval suggests that 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. The 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 the subjects are selected for the study). For example, a common type of information bias in case-control studies is recall bias. One may compare the patients with an FQREC HAI to a random sample of noninfected controls in an effort to identify the risk factors for FQREC HAI. If the patients with an FQREC HAI are aware of their diagnosis, they may be more likely to try to identify the 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 HAI will be spuriously strengthened.
bias (i.e., distortion in the estimate of effect resulting from the manner in which the subjects are selected for the study). For example, a common type of information bias in case-control studies is recall bias. One may compare the patients with an FQREC HAI to a random sample of noninfected controls in an effort to identify the risk factors for FQREC HAI. If the patients with an FQREC HAI are aware of their diagnosis, they may be more likely to try to identify the 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 HAI 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 a bias may exist, one must also consider the likely impact of the bias on the study results. The 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 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 HAI and mortality, one must consider the underlying severity of illness as a potential confounder. Patients with more severe illness are more likely to develop FQREC HAI. 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 is also important to consider the potential for confounding variables in the design of the study.
TABLE 9.1 Hierarchy of Quasi-Experimental Study Designs | ||||||||||||||||||||||||||||
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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 (15). This design is also frequently referred to as a “before-after” or “pre-post intervention” study (16,17
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