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 3–6 surveyed the four observational designs and showed that each one is built on the same kind of 2×2 table with the same kind of measure of association. The unstated assumption running through all of those lessons is that the variables in the table actually mean what we think they mean — that “exposure” really is exposure, “disease” really is disease, and the chosen confounders are the right ones in the right relationship to the exposure and outcome. Lesson 7 stops to interrogate that assumption. The three content sections each pick at a different layer of it: Section 1 asks whether our instruments measure the constructs we say they measure (and whose theory of disease determined what got measured at all); Section 2 uses directed acyclic graphs to expose the most common causal-specification mistakes — conditioning on colliders, adjusting for mediators, and the “paradoxes” both produce; Section 3 works through three biases that survive even careful measurement and adjustment — residual confounding, reverse causation, and simultaneity. By the time you reach Lesson 8 (sampling and selection), the inventory of biases this lesson opens will be ready to be combined with the additional biases that arise from who ends up in the study at all.

Why Measurement Matters in Epidemiology

Epidemiological research depends on our ability to accurately measure the constructs we study—exposures, outcomes, and confounders. When measurements fail to capture the underlying phenomenon of interest, even a perfectly designed study can yield misleading results. This section examines how measurement problems introduce systematic error into epidemiological research.

Click each card below to explore the core measurement concepts that underpin epidemiological research.

Theory Before Instruments: How Frameworks Shape What We Measure

Construct validity asks whether an instrument captures the construct it is supposed to measure. A prior question is rarely asked but more consequential: where does the construct come from? Every variable in an epidemiological study is the residue of a theoretical decision—a claim about what causes disease, what counts as a relevant exposure, and where the boundary of the “cause” should be drawn. That decision is upstream of any psychometric work, and it determines what the rest of the analysis can possibly see.

Public health has historically been dominated by the biomedical model, which locates disease in individual bodies and explains population patterns as the aggregation of individual risk factors. The biomedical model is powerful for some questions (it gave us germ theory, vaccines, antibiotics), but it systematically under-measures the conditions in which bodies live, work, and age. Several theoretical frameworks have emerged to push back against this narrowness.

The four frameworks above name competing theories of what causes disease. The next case studies move from theory to instrument, showing how widely-used measurement tools quietly inherit the assumptions of whatever theory built them.

Case Study: The CES-D Scale and Differential Item Functioning

The CES-D case showed how a multi-item instrument can mean different things in different groups. The next example takes the same lesson to its limit: a single-item measure that turns out to be one of the strongest predictors in epidemiology — and to inherit all the same problems.

Self-Rated Health: A Deceptively Simple Measure

Self-rated health (SRH)—typically measured as a single item (“How would you rate your overall health?”)—is one of the strongest predictors of mortality in epidemiological research. Yet SRH responses are shaped by comparison groups, expectations, and cultural frameworks.

Validity questions about what we are measuring naturally lead to a related question about the scale on which we record the answer. Most epidemiological surveys use ordinal Likert-type response options; almost every analysis treats them as if the gaps between categories were equal. They usually are not.

The Problem of Scale Level: Ordinal vs. Interval

Epidemiological and health behavior research frequently uses Likert-type scales—ordinal response options such as “Strongly Agree” to “Strongly Disagree.” Researchers routinely assign numeric values (1–5) and analyze these as if the intervals between categories are equal. But is the “distance” between “Strongly Agree” and “Agree” really the same as between “Neutral” and “Disagree”?

Construct validity, response-scale form, and cultural invariance are all about whether the instrument is asking the right thing. The last measurement issue this section covers is about whether it is asking it consistently.

Reliability and Attenuation Bias

Even when a measure is conceptually valid, poor reliability introduces random measurement error that systematically weakens (attenuates) observed associations. This is one of the most pervasive yet underappreciated problems in nutritional epidemiology.

set.seed(230)
n <- 2000

# True exposure X, outcome Y with true slope = 1
X <- rnorm(n, mean = 10, sd = 2)
Y <- 2 + 1*X + rnorm(n, sd = 1)

# Noisy version of X (e.g., FFQ-measured dietary intake)
X_noisy <- X + rnorm(n, sd = 2)

# Compare slopes from "perfect" vs "noisy" exposure
coef(lm(Y ~ X))["X"]               # expect ~1.00 (truth)
coef(lm(Y ~ X_noisy))["X_noisy"]   # expect < 1.00 (attenuated)

# Stretch: how does noise size change the attenuation?
sds <- c(0, 0.5, 1, 2, 4)
sapply(sds, function(s) {
  Xn <- X + rnorm(n, sd = s)
  unname(coef(lm(Y ~ Xn))[2])
})

Introduction and Overview

Section 1 asked whether the variables in the table mean what we think they mean. This section asks whether we have put them in the right relationship to one another. The mistakes covered here — conditioning on colliders, adjusting for mediators, mis-specifying the causal structure — do not show up in measurement error or sample size. They are mistakes about which variables to control for, and they can flip the sign of a true causal effect even when every measurement is perfect — the formal language for these decisions is the potential-outcomes framework (Rubin, 1974; Holland, 1986). The standard tool for thinking through these decisions is the directed acyclic graph (DAG); the standard takeaway is that more adjustment is not always better.

Directed Acyclic Graphs (DAGs) for Causal Reasoning

A directed acyclic graph (DAG) (Pearl, 1995) is a visual tool that represents causal assumptions about the relationships among variables. Each arrow indicates a hypothesized direct causal effect. DAGs help researchers identify which variables to adjust for—and, critically, which variables should not be adjusted for—to obtain unbiased causal estimates. The accordion below works through three canonical cases — confounding (where adjustment removes bias), collider bias (where adjustment creates it), and mediator adjustment (where adjustment removes part of the very effect you are trying to estimate). After the worked examples, the interactive playground that follows lets you build each pattern by clicking variables to adjust or not.

The simulator builds the abstract patterns. The two case studies below show those patterns in action in the published literature: each “paradox” turns out to be the literature's name for what happens when investigators adjust for the wrong variable.

Case Study: The Obesity Paradox

The obesity paradox is a collider problem. The next case is the closely related — and in some ways even more pernicious — mediator problem.

Case Study: Overadjustment Bias in Perinatal Epidemiology

Introduction and Overview

Section 1 covered measurement; Section 2 covered the structure of the causal model. This section addresses three biases that survive both. Residual confounding remains even after correct DAG specification, because we never measure confounders perfectly. Reverse causation arises when the apparent cause is actually downstream of the apparent effect. Simultaneity is the limit case where two variables cause each other and the very framing of the analysis is wrong. All three are common enough in the published literature that you will encounter examples within a few weeks of any reading list.

Residual Confounding

Residual confounding occurs when adjustment for a confounder is incomplete—either because the confounder is measured imprecisely, categorized too coarsely, or only partially captured by the available variables. Even when researchers “adjust for” a confounder, residual confounding can persist and bias effect estimates.

Residual confounding is what is left over after we have tried to adjust for the variables we know about. The next bias is what happens when our entire ordering of cause and effect is wrong.

Reverse Causation

Reverse causation occurs when the presumed outcome actually causes (or influences) the presumed exposure, rather than the other way around. This is particularly problematic in cross-sectional and case-control studies where the temporal sequence of events is unclear.

Reverse causation flips the direction of a single arrow. The third bias goes one step further: it allows arrows in both directions at once.

Simultaneity Bias

Simultaneity bias (also called bidirectional causation) arises when two variables mutually cause each other, making it impossible to identify the causal direction from observational data alone. Standard regression models assume that the predictor causes the outcome, not vice versa; when causation runs in both directions, ordinary regression estimates are biased.

Bringing It All Together

This lesson took apart three of the deepest assumptions baked into every observational analysis: that the variables mean what we say they mean, that we have controlled for the right things in the right way (Hernán, 2004), and that the cause comes before the effect. Each section then built up the corresponding repertoire of biases — measurement (Section 1), causal-specification (Section 2), and the residual problems that survive both (Section 3). Together they form a checklist you can apply to any study you read for the rest of HSCI 230 and through HSCI 341 and 410.

The deeper move was the one Krieger and Link & Phelan have been making for decades: instruments do not pick themselves. Whether a study can “see” structural racism, neighbourhood disinvestment, occupational exposure, or chronic discrimination depends entirely on which theoretical framework chose its variables in the first place. A perfectly executed analysis of variables drawn from the wrong framework will reliably produce evidence that points away from the actual drivers of population health. That is why the conceptualisation step matters before the measurement step, and the measurement step before the causal-specification step.

Lesson 8 takes the next layer: who ended up in the study at all. Sampling, selection, and external validity are the biases that arise from which subjects we get to observe — biases that combine with the measurement and causal-specification problems documented here to produce the final, integrated picture of why an observational study’s causal claim might be wrong.

Final Reflection

This lesson took apart the assumptions baked into every observational analysis: that variables mean what we say they mean, that we have controlled for the right things in the right way, and that the cause comes before the effect. Each section then built up the corresponding repertoire of biases — measurement, causal-specification, and the residual problems that survive both. The reflection below asks you to put all three layers to work on a single hypothetical study; the comprehensive assessment that follows tests the conceptual material across the three sections.

set.seed(230)
n <- 2000

# True exposure X, outcome Y with true slope = 1
X <- rnorm(n, mean = 10, sd = 2)
Y <- 2 + 1*X + rnorm(n, sd = 1)

# Noisy version of X (e.g., FFQ-measured dietary intake)
X_noisy <- X + rnorm(n, sd = 2)

# Compare slopes from "perfect" vs "noisy" exposure
coef(lm(Y ~ X))["X"]             # expect ~1.00 (truth)
coef(lm(Y ~ X_noisy))["X_noisy"] # expect < 1.00 (attenuated)

## -----------------------------------------------------------------------------
## Stretch: how does noise size change the attenuation?
## -----------------------------------------------------------------------------
sds <- c(0, 0.5, 1, 2, 4)
sapply(sds, function(s) {
  Xn <- X + rnorm(n, sd = s)
  unname(coef(lm(Y ~ Xn))[2])
})
# Larger SD of measurement error -> larger attenuation toward zero.

Comprehensive Assessment

This 15-question assessment covers all topics from this lesson. You must score 100% to complete the lesson. Review the explanations for any incorrect answers and try again.