Which research situation below would an extraneous variable become a confounding variable?

Confounding

Confounding refers to differences in outcomes that occur because of differences in the baseline risks of the comparison groups. These differences may occur due to selection bias that distributes risk factors known as confounding variables unevenly between comparison groups. Confounding variables influences both the outcome variable and exposure variable causing a spurious association. For example, a comparison of mortality after open versus laparoscopic colectomy might be skewed because of the greater likelihood of open colectomy being performed as an emergency procedure in critically ill patients with perforation. In this example, the severity of the illness is a confounder in the observed association between mortality and surgical approach.

In evaluating the strength of evidence in a published study, readers must assess how well the researchers accounted for the potential effect of confounding. Confounding can be minimized in several ways, in both the design of the study and the analysis of the study’s results. In the design of a study, confounding is most effectively addressed with randomization. When subjects are randomized, potentially confounding variables (both recognized and unrecognized) are likely to be evenly distributed across comparison groups. Thus, whereas the baseline rate of outcomes in the entirecohort might be influenced by these factors, the differences across comparison groups are less likely to be affected.

When randomization is not practical, restriction or matching can be used to prevent confounding. Restriction refers to the tight control of study entry criteria, for example, only enrolling patients undergoing elective surgery and excluding emergent procedures. However, restrictive entry criteria can sometimes limit generalizability. In comparison, matching refers to using a comparison group of unexposed (control) subjects who are identical to the exposed (case) subjects across a set of characteristics (e.g., age, sex, residence) that have the potential to result in confounding.

In addition to minimizing confounding through good study design, confounding can also be addressed during the analytic phase of a study with statistical risk-adjustment techniques. The most common technique is multivariate regression analysis, including linear and logistic regression models. Logistic regression models are used when the outcome variable is binary, whereas linear regression is used when the outcome is continuous. Both of these approaches involve taking into account differences in the prevalence of recognized confounders across comparison groups. However, statistical risk adjustment has several important limitations. First, only recognized confounders can be addressed in the regression model. Second, every potential confounding variable added to a statistical model decreases the model’s statistical power and thereby increases the chance of resulting in a false-negative result (i.e., type II error). Third, regression model estimates are not very reliable when there are very few outcome events. As a rule of thumb, logistic regression must have at least 10 outcome events for every variable adjusted in the model, whereas linear regression requires 10–15 outcomes per variable included in the model to prevent overfitting.37,38

Confounding Variable.

If an extraneous variable is not appropriately controlled, it may be unequally present in the comparison groups. As a result, the variable becomes a confounding variable. In such cases, any differences between the two groups on a DV might very well be the result of the uncontrolled extraneous variable (i.e., confounding variable), because that variable has the effect of confusing, or confounding, proper interpretation of the study. The end result is that the true relationship between the IV and DV is somewhat disguised because of the possibility that another variable (the confounding variable) has influenced the outcome of the study in an unanticipated way. In the study by Chang et al., any one or more of the several demographic and obstetric features (e.g., maternal age, maternal weight, gestational age, newborn weight, and duration of labor) could function as a confounding variable if not adequately controlled.

Bias and Confounding

Bias occurs when “compared components are not sufficiently similar.”3 The compared components may involve any aspect of the study.Selection bias exists if there are systematic differences between people in the comparison groups. For example, selection bias may occur if, in comparing surgical resection to chemoradiation, oncologists avoid treating patients with kidney or liver failure. This makes the comparison biased because on average the surgical cohort will accrue more ill patients and this may influence survival or complication rates. This can be addressed through random assignment of participants to different treatment groups, known as randomization.Information bias exists if there are systematic differences in how exposures or outcomes are measured. Information bias can include observer bias, in which data are not collected the same way across comparison groups, and recall bias, in which inaccuracies of retrospective assessment can influence findings. Observer bias can be reduced by using blinded data collection, in which measurements are made without knowledge of which comparison group they are for; single blinding means participants do not know which group they are in, and double blinding means study staff who collect and/or interpret data do not know which study participants are in which group (until blinding is removed at the end). Recall bias can be reduced by using prospective data collection, in which measurements are made as participants move forward through time as opposed to attempting to remember what happened in the past.

Similar to bias,confounding also has the potential to distort the results. However, confounding refers to specific variables. Confounding occurs when a variable thought to cause an outcome is actually not responsible, because of the unseen effects of another variable. Consider the hypothetical (and obviously faulty) case where an investigator postulates that nicotine-stained teeth cause laryngeal cancer. Despite a strong statistical association, this relationship is not causal, because another variable—cigarette smoking—is responsible. Cigarette smoking is confounding because it is associated with both the outcome (laryngeal cancer) and the supposed baseline state (stained teeth).

Confounders

A confounding variable (confounder) is a factor other than the one being studied that is associated both with the disease (dependent variable) and with the factor being studied (independent variable). A confounding variable may distort or mask the effects of another variable on the disease in question. For example, a hypothesis that coffee drinkers have more heart disease than non-coffee drinkers may be influenced by another factor (Figure 3.10). Coffee drinkers may smoke more cigarettes than non-coffee drinkers, so smoking is a confounding variable in the study of the association between coffee drinking and heart disease. The increase in heart disease may be due to the smoking and not the coffee. More recent studies have shown coffee drinking to have substantial benefit in heart health and in the prevention of dementia.

In public health, researchers are often limited to observational studies to find evidence of causal relations. Experimental studies may not be possible for many technical, ethical, financial, or other reasons. The proper causal interpretation of the relations from carefully developed epidemiological studies is vital to the development of effective measures of prevention.

Confounding

Confounding is a type of systematic error that can be present in observational research studies.38,40,41 Confounding occurs when two factors are associated with each other, and the effect of one factor on a given outcome is distorted by the effect of the other factor. Randomized clinical trials of sufficient size generally are usually not confounded because randomization itself should lead to an equal distribution of confounding factors among various treatment groups.6

An example that illustrates possible confounding comes from observational studies of indomethacin for tocolysis. Norton and colleagues performed a matched retrospective cohort study of infants delivered at less than 30 weeks' gestation.42 The authors identified 57 infants delivered at or before 30 weeks' gestation whose mothers were exposed to indomethacin for preterm labor and 57 infants whose mothers did not receive indomethacin. Infants born to mothers treated with indomethacin before delivery had a higher rate of necrotizing enterocolitis and grades II to IV intraventricular hemorrhage, an observation also noted in other observational studies.43–45 However, the proper interpretation of observational studies requires that potential sources of systematic error such as confounding and bias be considered. In this example, it is possible that confounding may explain the association between indomethacin and the neonatal morbidity observed in this observational study.46 Specifically, because indomethacin is generally not a first-line tocolytic in practice, it is likely that this drug was used mainly in subjects who failed first-line tocolysis. If failing first-line tocolysis is itself a risk factor for adverse neonatal outcome, the association between indomethacin and adverse neonatal outcome can be confounded. Thus a principal question in the interpretation of these studies is whether patients who are failing first-line tocolysis are themselves at higher risk for adverse neonatal outcomes (whether exposed to indomethacin or not) than are patients who respond to first-line tocolysis. Existing data suggest that women whose labor does not stop after first-line tocolysis have an increased risk for adverse neonatal consequences because of the well-established relationship between tocolytic failure and subclinical and intraamniotic infection, both of which are associated with adverse neonatal outcome.

Because of the relationships between refractory preterm labor and subclinical infection and between subclinical infection and major neonatal morbidity,47–49 it is uncertain whether the association between indomethacin and adverse neonatal outcome in these retrospective observational studies is a true association or a spurious association resulting from confounding. We hypothesize that in the observational studies, exposure to indomethacin may be nothing more than a sign of inflammation-driven preterm labor, which itself is associated with major neonatal complications.46

Drug adulteration

A potential confounding variable in studies of MDMA is that the subjects may not actually be taking MDMA, but rather other substances, such as amfetamine or metamfetamine. In 21 subjects who claimed to have taken only MDMA and no other drugs [183] a hair sample showed that 19 had MDMA present, while seven had concentrations of 3,4-methylenedioxyamfetamine (MDA) similar to or greater than those of MDMA. Eight subjects also tested positive for of amfetamine or metamfetamine. At a follow-up interview with those who tested positive for drugs other than MDMA, none admitted knowledge of taking MDA, amfetamine, or metamfetamine. These results suggest that not all street ecstasy tablets contain pure MDMA. Often, MDA, amfetamine, or metamfetamine is disguised as MDMA. It is unknown whether the combination of MDMA with these drugs poses a greater health risk to abusers. The main limitation of this study was that it relied on the subjects’ own reports. The authors suggested that hair testing be implemented in all MDMA research trials to ensure that the study sample is accurate.

3.7.2 Covariates

Covariates are confounding variables that may be related to a variable of interest but are not of interest in themselves. They can be statistically controlled for during analysis, which results in a more direct measurement of the relationship between the variables of interest. Typically, in neuroimaging studies age and sex are controlled for due to the known effects of these two variables on brain size143 (Barnes et al., 2010). In addition, in multi-site studies, site should be used as a covariate to control for effects of different MRI scanners on data. However, it should be noted that this does not fully account for effects of site, as sites are differentially affected by artifacts such as scanner drift, software upgrades and field inhomogeneity. Furthermore, often education is included as a covariate when examining relationships between neuroimaging measures and cognitive variables due to the relationship between education level and cognitive performance144 (Beeri et al., 2006). Other co-variates should be included in the analyses where appropriate.

One measure that is frequently discussed as a potential covariate in structural neuroimaging literature is total intracranial volume (TIV;145,143 Malone et al., 2015; Barnes et al., 2010). TIV acts as a proxy to “healthy” brain volume, since TIV measures the total intracranial space and has been demonstrated to remain constant despite increasing neural atrophy146,147 (Whitwell et al., 2001; Matsumae et al., 1996). By controlling for TIV, variables of interest can be compared while accounting for differences in brain morphometry due to head size. TIV can be measured via manual delineation of the region or automated measures, such as SPM, which have also been validated 145.

Elimination or Inclusion

To control directly the extraneous variables that are suspected to be confounded with the manipulation effect, researchers can plan to eliminate or include extraneous variables in an experiment. Control by elimination means that experimenters remove the suspected extraneous variables by holding them constant across all experimental conditions. In the treatments-effect study described earlier, researchers examined the effects of a treatment program for people checked into substance-abuse facilities. If the researchers suspected that the gender of the therapist might be confounded with the effects of the treatment, they could use the same male (or female) therapist in both treatment conditions. As a result, any potential effect caused by the gender of the therapist is converted to a constant in both conditions.

In contrast to control by elimination, researchers can include the suspected extraneous variables in an experiment. If researchers suspect the gender of the therapist is an extraneous variable, they can include the gender of the therapist as an additional independent variable. Specifically, participants can be assigned to one of four experimental conditions: a treatment with a male therapist, a treatment with a female therapist, a placebo control with a male therapist, and a placebo control with a female therapist. This experimental design enables consideration of the effect of the treatment, the effect of the therapist's gender, and the interaction of both independent variables.

9.1 Nested or Hierarchical Designs

It is not unusual for extraneous variables to be ‘nested.’ For example, if subjects are recruited and tested separately at different testing centers, the subjects are ‘nested within testing center.’ If subjects are animals such as mice or piglets, then the subjects are naturally nested within litters, which are nested within parent, which may be nested within laboratory. The nesting information can be used in matched designs, since the nesting forms natural groupings of like subjects. For within subjects designs, the nesting information can be used during the analysis for examining the different sources of extraneous variation (e.g., Hierarchical Models: Random and Fixed Effects). Designs in which different levels of nesting are assigned different treatment factors are called ‘split-plot designs’ (see Sect. 9.2).

A second type of nesting is a nesting structure within the treatment factors being examined. Examples given by Myers (1979) include memorization of words within grammatical class; time taken to complete problems within difficulty levels. Models and analyses used in such experiments must reflect the nested treatment structure.

Introduction

Controlling for large numbers of confounding variables is often necessary for estimating valid exposure effects in post-authorization safety studies (PASS) that utilize health-care databases such as administrative claims and electronic medical record (EMR). Standard methods for confounding control have traditionally relied on multivariable regression models. Although useful for many situations, correct use of these models can be challenging for PASS, involving large numbers of covariates. In these settings, explicitly modeling the modification of exposure effects by baseline covariates to account for exposure effect heterogeneity can be difficult and substantially increases the likelihood of model misspecification (Cochran, 1969; Sturmer et al., 2006; Arbogast and Ray, 2009). Challenges in identifying areas of nonoverlap in covariate support across exposure categories can further create problems with estimation of exposure effects by regression models (Patorno et al., 2013). To address these challenges, methods that collapse the information of a large set of covariates into a single value or summary score, and then use this summary measure to assess areas of nonoverlap in covariate support, control for confounding, and evaluate effect modification have become increasingly popular.

As discussed in Chapter 5.1, exposure propensity scores (EPS) technique has been the most widely used summary measure and has become a standard tool for confounding control in pharmacoepidemiologic studies, including PASS (Rosenbaum and Rubin, 1983; Sturmer et al., 2006). An alternative summary score to EPS is the prognostic scores technique, often referred to as disease risk scores (DRS). Instead of summarizing covariate associations with exposure, DRS act as “prognostic balancing scores” by summarizing covariate associations with potential outcomes (Hansen, 2008).

The idea of using an outcome summary measure to control for confounding was introduced several decades before the advent of EPS (Belson, 1956; Peters, 1941). The proposed method included fitting a risk model within the control population and then using the predicted values from this fitted model as a way to reduce dimensionality when matching. Later, it was proposed to stratify on a “multivariate confounder score” by fitting an outcome model to the full study population as a function of baseline confounders and exposure, and then assigning risk scores after setting exposure status to zero (Miettinen, 1976).

Despite the early introduction of using risk summary measures for confounding control, their use was impeded in part because of a simulation study that examined their statistical properties, which demonstrated that adjustment for DRS can result in exaggerated statistical significance of effect estimates (Pike et al., 1979; Arbogast and Ray, 2009). However, after reexamining these findings, it was found that this exaggeration is small except when there is a very strong correlation between confounders and exposures (correlation coefficient exceeding 90%) (Cook and Goldman, 1989; Arbogast and Ray, 2009, 2011). These settings are uncommon in practice and result in poor exposure equipoise, limiting the ability to conduct valid analyses to begin with (Cook and Goldman, 1989; Arbogast and Ray, 2009; Patorno et al., 2013). It was further explained that this exaggerated statistical significance is not a property of DRS themselves, but a result of model misspecification and overfitting that can occur when fitting the DRS model (Hansen, 2008; Leacy and Stuart, 2014).

Recently, it was shown that DRS act as prognostic balancing scores that can yield valid effect estimates with causal interpretations. Due in part to this recent theoretical work, there has been an increased interest in the application of DRS for confounding control with a recent surge in the number of applications of DRS in drug safety research (Arbogast and Ray, 2009; Cadarette et al., 2010; Wyss et al., 2014, 2015; Kumamaru et al., 2016a,b). They have also become increasingly used in clinical medicine to direct treatment decisions and evaluate exposure effect heterogeneity (Teasdale and Jennett, 1974; Knaus et al., 1991; Gail et al., 1999; Lyden et al., 1999; Freedman et al., 2011; Wang et al., 2016).