This glossary collects the key concepts, people, and ideas you will meet in this lesson. Use it as a reference while you work through the material, or as a review before assessments. Type in the search box to filter entries.

Introduction and Overview

Lessons 7–10 worked through bias one category at a time. This lesson finishes the inventory by addressing the third leg of the canonical bias triad — confounding — and then steps back to the statistical-inference issues that turn even unbiased estimates into wrong conclusions. The two content sections divide the work cleanly. Section 1 takes confounding from the textbook definition through pharmacoepidemiology's standard nightmare (confounding by indication), through the more advanced problem of time-varying confounding, into the harder theoretical question of whether constructs like race or income are confounders to be controlled or structural exposures to be measured. Section 2 turns to the analytic issues that haunt even well-adjusted models: model misspecification, multicollinearity, Type I/II errors, Simpson's paradox, the ecological fallacy, the modifiable areal unit problem, and missing data. By the end, the toolkit needed for Lesson 12's integrated appraisal will be complete.

What Is Confounding?

Confounding occurs when a third variable—the confounder—is associated with both the exposure and the outcome, distorting the observed relationship between them. Unlike mediators (which lie on the causal pathway), confounders represent alternative explanations for an association. If unaddressed, confounding can make a harmful exposure appear protective, a beneficial treatment appear harmful, or a null relationship appear significant.

Classic Case: Hormone Replacement Therapy

One of the most consequential examples of confounding in modern epidemiology involves hormone replacement therapy (HRT) and cardiovascular disease (CVD) risk in postmenopausal women. For decades, observational studies consistently suggested that HRT reduced CVD risk by 30–50%. These findings influenced clinical guidelines worldwide.

set.seed(230)
n <- 5000
ses <- rbinom(n, 1, 0.5)                                  # 1 = high SES
hrt <- rbinom(n, 1, prob = ifelse(ses == 1, 0.6, 0.2)) # high SES uses HRT more
# CVD risk: lower in high SES, NOT affected by HRT (true null)
cvd <- rbinom(n, 1, prob = ifelse(ses == 1, 0.05, 0.15))

# Crude (unadjusted) OR -- looks "protective"
exp(coef(glm(cvd ~ hrt, family = binomial))["hrt"])

# Within each SES stratum -- the true effect: ~1.0
tapply(seq_len(n), ses, function(i) {
  exp(coef(glm(cvd[i] ~ hrt[i], family = binomial))[2])
})

# Adjusted OR, controlling for SES
exp(coef(glm(cvd ~ hrt + ses, family = binomial))["hrt"])

The HRT case is the textbook example of confounding by lifestyle and SES. The next form — confounding by indication — is the most pervasive issue in observational pharmacoepidemiology, and the reason any drug-effect estimate from administrative data should be read with care.

Confounding by Indication

Confounding by indication is a specific form of confounding that arises in pharmacoepidemiological studies when the reason a treatment is prescribed (the “indication”) is itself a risk factor for the outcome. Because sicker patients are more likely to receive treatment, naive comparisons of treated vs. untreated patients systematically overestimate harm or underestimate benefit. The three flip cards below show the standard scenario, its mirror image (confounding by contraindication), and the design tools used to address both.

Confounding by indication is hard but at least the confounder sits at baseline. Time-varying confounders make the problem one step worse: they evolve, and their values feed back from prior treatment.

Time-Varying Confounding

Time-varying confounding occurs when a confounder changes over time and is simultaneously affected by prior treatment and predictive of future treatment and outcome. This creates a feedback loop that standard regression cannot resolve.

Marginal structural models handle the technical problem of time-varying confounding within a single causal pathway. The next subsection addresses a deeper question that no analytic technique alone can resolve: whether some of the variables we routinely treat as confounders should be reframed as the very exposures we ought to be measuring.

Beyond “Controlling For”: Intersectionality and the Limits of Variable-by-Variable Adjustment

So far this lesson has treated confounding as a problem with a technical solution: identify the confounders, adjust for them, and proceed to the “true” effect. That logic works well for the kind of variable a randomised trial would have balanced—a clinical comorbidity, a baseline lab value, a discrete behaviour. It works less well, and sometimes badly, when the “confounder” is not really a variable at all but a structural process that produces both the exposure and the outcome over the lifecourse.

Race is not a confounder; racism is an exposure

A standard Table 1 in an epidemiological paper presents race/ethnicity as a baseline characteristic to be adjusted for. But race itself does not have a biological mechanism that causes hypertension, low birthweight, or COVID-19 mortality. What does the causing is racism—experienced across a lifecourse as residential segregation, job market discrimination, biased policing, differential medical treatment, and chronic vigilance—all of which become biologically embodied (Williams, Lawrence, & Davis, 2019; Krieger, 2014).

When researchers “control for race,” they often inadvertently obscure the structural process they should be measuring. Worse, adjusting for downstream consequences of racism (income, education, neighbourhood) can constitute over-adjustment bias, partialling out the very mediators through which the structural exposure operates (VanderWeele & Robinson, 2014; Schisterman, Cole, & Platt, 2009). The variable is in the model; the explanation has been removed.

Intersectionality and the additivity assumption

Crenshaw’s (1989) concept of intersectionality began in legal theory with a simple observation: a Black woman’s experience of discrimination is not the sum of “being Black” plus “being a woman.” The intersections produce qualitatively distinct exposures that neither single-axis category, nor an additive combination of them, can capture.

Standard regression, by default, models adjustment as additive: the coefficient on race is interpreted as the effect “holding gender, class, and other variables constant.” Bauer (2014) shows why this is theoretically inadequate for studying inequality. Holding gender constant while estimating a racial effect implicitly imagines a population in which racial categorisation is detached from gendered experience—a counterfactual that does not, in any meaningful sense, exist. Quantitative researchers can address this with explicit interaction terms, stratified analyses, intersectional MAIHDA (multilevel analysis of individual heterogeneity and discriminatory accuracy; Evans et al., 2018), or descriptive analyses that report rates within intersecting groups rather than coefficients adjusted across them.

When biomedical models fall short

The biomedical model is comfortable with confounders that are themselves biomedical: cholesterol confounding the diet–CHD relationship, age confounding most things. It becomes unstable when the “confounder” is the social structure itself—because that confounder operates over decades, through dozens of mediating mechanisms, with effects that change as societal conditions change. Fundamental cause theory predicts exactly this: as one mechanism is closed off (e.g., smoking is reduced), the social gradient in mortality reappears through whatever mechanism is currently relevant (e.g., obesity, opioid overdose). The pattern is robust to mechanism-by-mechanism adjustment because the cause is upstream of any specific mechanism (Link & Phelan, 1995; Phelan et al., 2010).

Introduction and Overview

Section 1 closed the bias inventory. Even after every bias has been addressed, an analysis can still produce wrong conclusions if the statistical model itself does not fit the data, or if the inferential framework is misused. This section walks through seven such issues in order: model misspecification, multicollinearity, Type I/II errors, Simpson's paradox (with a hands-on simulator), the ecological and atomistic fallacies (callbacks to Lesson 6), the modifiable areal unit problem, and missing data. Each is short on its own, but together they constitute most of the analytic mistakes that survive peer review.

Model Misspecification

A statistical model is misspecified when the assumed functional form does not reflect the true relationship between variables. One of the most common errors is assuming a linear relationship when the true relationship is nonlinear.

Multicollinearity

Multicollinearity occurs when two or more predictor variables in a regression model are highly correlated. This does not bias coefficient estimates but dramatically inflates their standard errors, making individual effects unstable and difficult to interpret.

Type I and Type II Errors

Type I error (false positive) is the probability of concluding an effect exists when it does not. Type II error (false negative) is the probability of failing to detect a real effect. These errors trade off: making it harder to achieve significance (lower alpha) reduces Type I error but increases Type II error, especially in small samples.

Simpson’s Paradox

Simpson’s paradox occurs when a trend that appears in aggregated data reverses when the data are stratified by a confounding variable. The paradox highlights the danger of drawing causal conclusions from aggregate statistics without considering underlying group structure.

The reversal occurs because Treatment X was disproportionately assigned to severe cases (which have worse outcomes regardless of treatment). The aggregated data hides this confounding by severity, producing a misleading conclusion. The correct causal interpretation requires stratification.

Simpson's paradox is what happens when stratification reveals confounding at the individual level. The complementary problem is what happens when we move between levels of analysis — from groups to individuals or vice versa. Lesson 6 introduced this material in detail; the next two subsections recall the essentials.

Ecological Fallacy and Atomistic Fallacy

Modifiable Areal Unit Problem (MAUP)

The modifiable areal unit problem is a form of the ecological fallacy specific to spatial analysis. When individual-level data are aggregated into geographic units (census tracts, counties, provinces), the choice of unit size and boundary definitions can alter statistical results—sometimes dramatically.

The ecological-fallacy and MAUP issues arise from how the data were assembled. The last analytic problem in this section is what to do when those data have holes in them — a near-universal problem whose handling can either preserve or wreck a study's conclusions.

Missing Data

Missing data are ubiquitous in epidemiological research. The validity of analysis depends critically on the mechanism underlying missingness; the modern taxonomy of MCAR / MAR / MNAR was set out by Rubin (1976):

Bringing It All Together

This lesson completed the bias inventory of HSCI 230 by closing out confounding (Section 1) and the analytic issues that survive even unbiased data (Section 2). The HRT / WHI story made vivid how confounding can reverse the direction of a clinical recommendation, while confounding by indication and time-varying confounding showed why specialised tools — restriction, active comparators, marginal structural models — are part of the modern epidemiologist's repertoire. The lesson also pushed past the conventional “variable-by-variable adjustment” framing to ask harder theoretical questions about whether race, gender, and SES belong in models as confounders to be controlled or as structural exposures to be measured.

Section 2 then walked through the analytic problems that remain even after confounding has been handled: model misspecification, multicollinearity, Type I/II error and the winner's curse, Simpson's paradox, the ecological and atomistic fallacies, the modifiable areal unit problem, and missing data. These issues are the most common reasons a result fails to replicate, and recognising them is the last skill the course owes you before the integrated appraisal of Lesson 12. The reflection below asks you to apply the full bias inventory to a study of your choice; the final assessment then tests the conceptual material before Lesson 12 integrates the entire course into a single critical-appraisal exercise.

set.seed(230)
n   <- 5000
ses <- rbinom(n, 1, 0.5)                                   # 1 = high SES
hrt <- rbinom(n, 1, prob = ifelse(ses == 1, 0.6, 0.2))     # high SES uses HRT more

# CVD risk: lower in high SES, NOT affected by HRT (true null)
cvd <- rbinom(n, 1, prob = ifelse(ses == 1, 0.05, 0.15))

# Crude (unadjusted) OR -- looks "protective"
exp(coef(glm(cvd ~ hrt, family = binomial))["hrt"])

# Within each SES stratum -- the true effect: ~1.0
tapply(seq_len(n), ses, function(i) {
  exp(coef(glm(cvd[i] ~ hrt[i], family = binomial))[2])
})

# Adjusted OR, controlling for SES
exp(coef(glm(cvd ~ hrt + ses, family = binomial))["hrt"])