Misnomers regarding terminology appear to be particularly common in conjunction with studies that examine outcomes of infections and other adverse events. If patients with a healthcare-associated infection are being compared to patients without healthcare-associated infection with respect to an outcome such as length of stay, mortality, or medical costs, a cohort study is being conducted, assuming that patients are selected on the basis of the presence or absence of infection. The infection constitutes the exposure. Similarly, studies in which outcomes of patients with a resistant microorganism are compared with outcomes of patients with the susceptible form of the microorganism are following a cohort design. If exposed and nonexposed subjects are matched on other criteria, such as age and severity of illness, the study is a matched cohort study. The distinction between matched cohort and matched case-control studies is not just a semantic one. In a matched case-control study, it is necessary to perform a matched analysis if the matching factors are associated with exposure, even if they are not associated with the outcome, whereas in a matched cohort study, this requirement does not exist (13).

Abundant examples exist in which the terms case and control are used in the context of a matched cohort study, leading to confusion about the study design (14). For instance, a study (15) about the “attributable mortality rate” of bacteremia due to methicillin-resistant Staphylococcus aureus (MRSA) claimed to perform a “retrospective cohort analysis and two independent case-control analyses.” As outlined above, this terminology is incorrect, since in all three analyses, outcomes were compared, and thus, the term matched cohort studies would have been more appropriate.

Perhaps nowhere is terminology in healthcare epidemiology more confusing than in the use of the word attributable (16,17). This word is included in a myriad of epidemiologic
terms with meanings that vary widely. The dictionary definition of attributable is “ascribed to” and, in epidemiology, it is frequently taken to be synonymous with “caused by.” However, there are two types of causation that are often not distinguished. During a defined follow-up period, an exposure may either shorten the interval to occurrence of disease or cause a disease case to occur that otherwise would not have occurred (18). The former is an accelerated disease case, whereas the latter is an excess case. If exposure prevents disease, this may be restated to indicate that exposure either lengthens the interval to occurrence of disease or averts a case from happening that otherwise would have occurred.

The rationale for constructing formulas to measure the attributable fraction is that not all disease in exposed patients is necessarily due to exposure: some exposed individuals would have developed disease, even at the same time, if they had not been exposed. It is also evident that the ratio of exposed patients belonging to these two causal types, accelerated or excess cases, depends on the duration of the follow-up. It can be shown that, compared to the enumeration of excess cases, deriving an estimate of the number of accelerated cases relies on additional, more tenuous assumptions about the form of the causal relationship between exposure and disease. Hence, rather than attempting to estimate the fraction of exposed cases that are caused by exposure, it is generally preferred to restrict attention to excess cases. The occurrence of excess cases can be estimated by simply comparing the incidence proportion in exposed individuals to the incidence proportion in nonexposed individuals, assuming that confounding is absent. Due to these considerations, Greenland and Robins (19,20) recommend the use of the term excess fraction in place of attributable fraction when the objective is to quantify the fraction of exposed cases that are excess cases caused by exposure. They reserve the term etiologic fraction to indicate the proportion of exposed cases caused by exposure, including both types of causation. The population excess fraction is an estimate of the fraction of all cases in the population that are excess cases due to exposure. The set of terms that cover these concepts are referred to as the family of attributable fractions (13,19).

In contrast to the rich literature available in the field of chronic disease epidemiology, controlled studies aiming to determine the proportion of hospital deaths attributable to healthcare-associated infection are both rare and insufficient for the calculation of stable estimates (21). Furthermore, several methodological issues have to be considered, since the causal relationship between exposure to infection and death can be jeopardized by multiple confounders and biases (see example 3 below: Excess Mortality Due to MRSA Bloodstream Infection). Clearly, the choice of methods does matter when the excess burden of healthcare-associated infections needs to be assessed. For instance, in a recent cohort study by a French group investigating the outcome of 8,068 critically ill patients, the statistical association between intensive care unit (ICU)-acquired infection and mortality tended to be less pronounced in findings based on the population excess fraction than in study findings based on estimates of relative risk (17).

The surgeon who explains that the reason his or her patients have a higher infection rate is that he or she operates on sicker patients demonstrates an informal grasp of the concept of confounding. However, when it is necessary to conduct and analyze an epidemiologic investigation, this intuitive understanding of confounding reveals its limitations. We begin by offering two core principles that may run somewhat counter to conventional wisdom:

Confounding is present when there is discordance between the true causal effect of an exposure on the outcome in a target population and the measured association between exposure and disease (23). Thus, an exploration of confounding starts with an exposition on causation. What is meant by true causal effect?

Causation is best understood in terms of the question: What would have happened if the exposure had not occurred? Stated another way, the causal effect of exposure in exposed individuals is represented by the difference between their actual disease status and what would have happened if everything else had been the same up until the time of exposure, but that they had then not been exposed or exposed to a different degree in the latter scenario (23). Under this formulation, causation is defined on the basis of a comparison between outcomes under mutually exclusive conditions: exposed and unexposed or, alternatively, varied levels of exposure. However, in any single patient, only one of these conditions is observed. In the absence
of time machines to replay experience under dissimilar exposure conditions, a straightforward way to directly measure causal effects is not available. When exposure is randomly allocated, it is possible to derive an estimate of the unconfounded, average causal effect of exposure, with a random error correlated with sample size. In the absence of random allocation of exposure, causal inference relies on untestable beliefs regarding causal relationships and unmeasured confounders (24).

It is useful to depict assumptions about causal relationships in a graphical format to identify potential sources of confounding. The causal effects of exposure on disease may be visualized as arrows aiming from exposure to disease (Fig. 88-1). These arrows represent the postulated causal mechanisms or pathways by which exposure affects the outcome or disease. Causal pathways that link exposure (E) and disease (D) may be direct or indirect. An indirect pathway is characterized by the presence of an “intermediate variable” (I) that mediates a causal effect, whereas a direct effect lacks an intermediate variable. The causal null hypothesis is the assumption that there are no indirect or direct causal pathways pointing from exposure to disease. Graphical representations of causal relationships are called directed acyclic graphs (25,26).

Confounding arises when direct or indirect causes of exposure are also direct or indirect causes of disease status. When exposure is a type of treatment and confounding is due to factors that influence treatment selection, the term confounding by indication is sometimes used (27,28). Causes of exposure can be visualized as arrows pointing toward exposure. If these inputs into exposure also have outputs connecting to disease through paths that do not include exposure, noncausal pathways from exposure to disease exist. The labeling of a pathway as noncausal is done from the perspective of exposure and disease. If research questions pertain to multiple exposures, the postulated connections between each factor of interest and disease may, in turn, be divided into causal or noncausal pathways. Noncausal pathways create an association between exposure and disease, one that is not a consequence of exposure, hence the need to block the noncausal pathways if the goal is to estimate the true causal effects of exposure. Factors located within these noncausal pathways are usually associated both with exposure and disease, although in any given study these associations may themselves be obscured by confounding, and therefore, not manifested (23,29).

Successful randomization eliminates confounding by breaking the causal inputs into exposure or treatment. It makes the exposure or treatment actually received independent of what would have happened had exposure been absent or altered. This principle, which is surprisingly difficult to grasp, is another way to define the absence of confounding. The goal of epidemiology is to attempt to accomplish this feat with respect to measured confounders, using appropriate design and analytic strategies (29).

Perhaps what poses the most difficulty to individuals conducting epidemiologic research and readers of the literature is the myriad of statistical techniques available to analyze data. These statistical methods are not reviewed in detail here. Detailed recommendations for conducting methodologically sound multivariable analyses of observational studies have been summarized elsewhere (30,31). Rather, our goal is to emphasize the distinction between the statistical evaluation of association and the identification of confounding. Contrary to widespread belief, the p-value is not a useful test of confounding. Even the comparison of crude and adjusted measures of association is an inadequate approach by itself to detect confounding. Depending on the causal model, the adjusted measure of association may be more or less confounded than the crude measure. The judgment of whether an adjusted association is less confounded than a crude association relies on assumptions about the causal relationships between exposure, outcome, and the adjustment variables (32).

The first step toward reducing confounding in observational research on causal effects is to recognize its potential existence and to obtain measurements on potential confounders or to account for potential confounding during the design phase of the study. Sometimes these initial steps are omitted, as the following example illustrates.

Many investigators have examined the effect of antimicrobials on the subsequent occurrence of infection. Under certain conditions, systemic antibiotic use may decrease the risk of healthcare-associated infection. This has been demonstrated in clinical trials on ventilator-associated pneumonia (VAP) (33,34). An opposite effect of antimicrobial prophylaxis was suggested in a study that found that the duration of antimicrobial prophylaxis after major surgery was associated with a significantly increased risk of healthcare-associated BSI (35). The authors of this study observed six cases of BSI among 180 patients receiving short antibiotic prophylaxis, compared with 16 cases of BSI in 94 patients with extended antibiotic prophylaxis (crude odds ratio [OR], 5.9). These results were published without any consideration of the possibility of confounding.

In an observational study we conducted on the relationship between duration of antimicrobial prophylaxis and infections (36), we found a strong association between prolonged antibiotic prophylaxis and subsequent healthcare-associated BSI in the crude analysis. A total of 2,641 patients undergoing cardiac surgery were included in the study, divided into those in whom antimicrobial prophylaxis was short (<48 hours) and those in whom antibiotic prophylaxis was prolonged (>48 hours) (36). The unadjusted analysis revealed an OR of 3.3, based on the
occurrence of 27 cases of healthcare-associated BSI (1.8%) after 1,478 procedures using short antibiotic prophylaxis compared with 65 cases of healthcare-associated BSI (5.7%) after 1,139 operations with prolonged antibiotic prophylaxis. The problem with this crude analysis was that the length of follow-up and ICU stay affected the likelihood of receiving prolonged antimicrobial prophylaxis.

Using survival analysis methods removed confounding related to differences in the length of follow-up; the apparent association appeared smaller (hazard ratio [HR], 1.7) based on Cox proportional hazards regression. Seventy-seven percent of cases of healthcare-associated BSI occurred in patients who stayed longer than 4 days in the ICU. Similarly, extended antibiotic prophylaxis was correlated with longer ICU stay. After stratifying for length of ICU stay, prolonged antibiotic prophylaxis was not associated with a significantly increased risk of BSI (HR, 1.4). In an additional analysis, we showed that prolonged antibiotic prophylaxis did not decrease the incidence of SSI; however, it increased the risk of isolation of resistant gram-negative bacteria and vancomycin-resistant enterococci (VRE) (37). In summary, these results demonstrate confounding of the crude association between prolonged antibiotic prophylaxis and healthcare-associated BSI by differences in follow-up and length of ICU stay (36).

Frequently, investigators do attempt to address confounding but use analytic methods that are suboptimal. A common error is to identify confounders primarily on the basis of the statistical significance of the association between the outcome and potential confounders. This strategy is inappropriate when the purpose of the regression model is to estimate the magnitude of the causal effect of an exposure on an outcome.

As an example, consider studies that have examined the impact of inadequate antimicrobial treatment of infection on patient outcomes (38, 39, 40 and 41). This is a research question that is not amenable to direct testing in a randomized trial, since it would be unethical to willingly expose patients to inappropriate treatment. To answer the question, therefore, we have to rely on observational studies. On the face of it, it is highly likely that inadequate antimicrobial therapy does have some negative effect on outcome in critically ill patients. The key objective of an observational study, then, is to remove as much of the confounding as possible so as to obtain an unbiased estimate of the magnitude of effect of inadequate therapy. In one such widely cited study of patients in the ICU with BSI, therapy was defined as inadequate if the antimicrobials being given to the patient were ineffective against the causative pathogen at the time that identification and susceptibility results were reported by the clinical microbiologic laboratory (42). The crude relative risk for mortality after inadequate therapy compared with adequate therapy equaled 2.2, corresponding to a crude OR of 4.1 (42). The “adjusted” effect estimate of inadequate antimicrobial treatment of BSI on hospital mortality had an OR of 6.9, after including the use of vasopressors, age, organ dysfunctions, and severity of illness, along with inadequate therapy, in a multivariable logistic regression model.

A major limitation with this analysis was that the factors included in the logistic regression model were only those found to be significantly associated with mortality. A stepwise variable selection approach was used with a p-value of .05 as the limit for the acceptance or removal of new terms. The problem is that this method does not remove confounding by factors not selected in the model. Many characteristics were identified that distinguished patients with inappropriate and appropriate antimicrobial use, such as time in the hospital prior to BSI, prior use of antimicrobials, and serum albumin. Presumably, these were factors that directly or indirectly influenced the probability that treatment was inadequate or were proxies for such factors. Some of these factors were also associated with the outcome but not always to a statistically significant degree. Not including these factors in the model likely contributed to an exaggerated estimate of effect (42).