Introduction &
Causal Concepts
Fundamental Epidemiological Concepts and Approaches
Learning objectives for this lesson:
- Describe what epidemiology is and trace how causal thinking developed, from miasma and germ theory through John Snow's cholera investigation to multicausal models of chronic disease.
- Distinguish inductive, deductive, and Bayesian reasoning, and describe the components of an epidemiologic study, from the source population to causal inference, naming selection bias and confounding as threats along the way.
- Read a directed acyclic graph (DAG): identify the exposure and the outcome, classify each other variable as a confounder (fork), a mediator (chain), a collider, or none of these, choose the adjustment set for a total effect, explain why conditioning on a collider (including restricting the sample) creates selection bias, and explain how a DAG differs from mediation analysis.
- Define necessary, sufficient, and component causes, classify the causes of a described disease using these terms, explain how the prevalence of causal complements changes the strength of association, and distinguish direct from indirect causes in a causal web.
- Use the Bradford Hill viewpoints, with temporality as the only strict requirement, to argue whether an observed association is likely to be causal.
- Explain the counterfactual (potential-outcomes) framework: state the counterfactual question for an exposed group, explain why individual causal effects cannot be observed and how a comparison group stands in for the missing outcome, define exchangeability, and explain why randomisation creates it.
- Define a confounder, explain why exchangeability is harder to assume in observational studies than in randomised trials, and describe how observational studies address confounding through restriction, matching, stratification, and multivariable adjustment, recognising that the modern analytic toolkit rests on the same counterfactual logic.
This course was developed by Dr. Kiffer G. Card based on Dohoo, I. R., Martin, S. W., & Stryhn, H. (2012). Methods in Epidemiologic Research. VER Inc.
Glossary: Key Terms, People & Concepts
📚 Reference page, available throughout the lesson
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.
What Is Epidemiology?
⏱ Estimated reading time: 10 minutes
Overview
Reading epidemiological research critically means evaluating study designs, identifying biases, and deciding what evidence to trust. This course moves from reading studies to producing them and teaches the methods themselves: how to design valid studies, calculate measures of disease frequency and association, work through screening tests, and conduct surveillance and outbreak investigations. The biases a critical reader looks for become the checklist a study designer works through. This lesson sets up the conceptual foundation: what epidemiology is, how scientific inference works (Susser & Susser, 1996), and what we mean when we say one thing “causes” another. It moves from the discipline's history, through the inferential logic that organises any study and formal models of causation, to the counterfactual framework that underpins modern causal inference. This first section defines epidemiology and its central goal, traces how ideas about the causes of disease changed from ancient Greece to the present, and looks at what John Snow's cholera investigation showed about preventing disease before its agent is known.
Learning Objectives
- 1.1 Define epidemiology and explain that its central goal is to identify causal associations between exposures and health outcomes in populations.
- 1.2 Describe how causal thinking about disease evolved, from Hippocratic and miasma theories through germ theory to multicausal models of chronic disease.
- 1.3 Explain what John Snow's cholera investigation showed about preventing disease before the causal agent is known.
1.1 What Epidemiology Studies and Why
Epidemiology is fundamentally about understanding the patterns, causes, and effects of health and disease in populations. Historically, epidemiologists have been concerned with identifying the "succession of events which result in the exposure of specific types of individuals to specific types of environment"; that is, the exposures and causal factors that drive disease. By this we mean that epidemiologists try to reconstruct the sequence that leads up to illness: which kinds of people come into contact with which conditions, and how that contact makes disease more or less likely. For example, the question is not only whether a toxin can damage the lungs, but which workers handle it, under what conditions, and how often they become ill as a result. Modern epidemiology aims to improve population health by integrating data from many disciplines and proposing interventions based on scientific evidence. The discipline focuses on identifying exposures, whether demographic factors, infectious agents, nutritional factors, toxins, or lifestyle elements, and evaluating their associations with health outcomes such as disease, quality of life, and mortality. Its central goal is to establish which of those associations are causal, because only a causal exposure gives prevention and policy something to act on. An association simply means that the exposure and the outcome tend to occur together; it does not tell us whether changing the exposure would change the outcome. For example, people who carry a lighter are more likely to develop lung cancer, but taking their lighters away would prevent nothing, because the lighter is only a marker of smoking. Removing a causal exposure, by contrast, does reduce disease, which is why the search for causes sits at the centre of the discipline.
Two features set the discipline apart from clinical medicine. The first is its unit of analysis. A clinician asks what is wrong with one patient and how to treat them, whereas an epidemiologist asks how an exposure and an outcome are distributed across a population and whether that pattern points to a cause. The second is that epidemiology is a field-based discipline. By this we mean that its evidence comes mainly from people living their ordinary lives, in homes, workplaces and communities, rather than from laboratories where conditions are controlled. This matters because in real life an exposure never acts alone. A person's diet, for instance, is tied up with their income, their neighbourhood, their work and their other habits, and all of these may affect their health at once. It is only by studying exposure-disease associations under these real-world conditions that we can begin to understand the web of causal relationships that affect health, and the associations we find are part of a complex web of relationships involving organisms and all aspects of their environment. A practical habit follows from both features: begin any study question by naming its exposure, its outcome and the population it concerns.
What counts as a cause, and how causes are found, has itself changed a great deal over the centuries, and the next subsection traces that history.
1.2 How Ideas About the Causes of Disease Changed
The way we think about what causes disease has shifted dramatically over the centuries (Susser & Susser, 1996a, 1996b), and understanding this history helps us appreciate the complexity of modern causal models. In broad outline, the earliest theories looked to the environment. The Hippocratic tradition blamed air, water and place, and miasma theory, dominant from about 1750 to 1885, blamed the bad air given off by decay; it was wrong about the mechanism, but the sanitary reforms it prompted still reduced infection. Germ theory in the late 1800s brought a one-agent, one-disease logic that led to major successes such as immunisation and specific treatment. By the mid-1900s, however, single agents could no longer explain rising chronic disease, and large population studies moved the field toward multifactorial models that combine biological, behavioural, social and environmental causes.
The eight cards below trace this evolution in chronological order, from Hippocrates around 400 BC to the One Health movement of the twenty-first century, and each one adds the people, studies and debates behind a turning point. Click each card to read its story. As you go, watch for one recurring tension: each era pulls between explaining disease at the level of individual mechanism (microbe, gene, biomarker) and explaining it at the level of populations and their environments.
(~400 BC)Click to learn more
(1750–1885)Click to learn more
(mid-1800s)Click to learn more
(late 1800s)Click to learn more
(early 1900s)Click to learn more
(mid-1900s)Click to learn more
(1970s)Click to learn more
(21st Century)Click to learn more
Read as a whole, the cards show two perspectives running side by side: one oriented toward biology and mechanisms of causation, the other toward populations and their interactions with the environment. Both are essential, and the modern position that emerges from their interplay is worth committing to memory.
Multiple Causes, Multiple Effects
Epidemiologists accept that there are multiple causes for almost every outcome and that a single cause can have multiple effects. The lack of one identifiable agent for a disease therefore does not mean that the disease has no identifiable causes.
Two of the cards, John Snow and Goldberger, show population reasoning running ahead of laboratory science, and the next subsection looks at what that achieved.
1.3 John Snow and Prevention Before the Agent Is Known
John Snow investigated cholera in London in the mid-1800s, while miasma theory still dominated and before germ theory had identified any agent. He combined three kinds of evidence: the geographical distribution of cholera cases, a series of observational studies, and a natural experiment comparing households supplied by two different water companies. The water-company comparison was the stronger part of this evidence, because a natural experiment compares households that were exposed or unexposed through circumstance rather than choice, which brings it closer to an experiment than a map of where cases clustered. From this evidence Snow concluded that cholera was spread by contaminated water, about 30 years before Koch isolated the organism Vibrio cholerae.
Snow's investigation demonstrates that disease can be prevented without knowing the proximal causal agent or its biological mechanism. Acting on the source of exposure, the contaminated water, could stop new cases even though nobody yet knew what in the water caused the illness. Goldberger's work on pellagra, described on its own card, makes the same point for a nutritional disease: in 1914 and 1915, improving the diet in two orphanages and part of an asylum almost eliminated pellagra among their residents (Goldberger, Waring, & Willets, 1915), more than twenty years before Elvehjem identified the missing nutrient, niacin, in 1937, although pellagra remained common in the southern United States until the 1940s (Frank, 2022). In both cases, careful observation of who became ill, and where, identified a cause and justified action before the agent was known.
This section has defined epidemiology, traced the shift from single-cause to multifactorial models of disease, and shown through Snow and Goldberger that prevention can come before knowledge of the agent. The key takeaways below summarise these points, and the next section turns to the logic of scientific inference.
Key Takeaways
- 1.1 Epidemiology is the study of how health and disease are distributed in populations and what determines that distribution. Its central goal is to identify causal associations between exposures (infectious agents, toxins, nutrients, lifestyle factors, social conditions) and health outcomes, so that prevention and policy have something to act on. What sets it apart from clinical medicine is that the unit of analysis is the population rather than the individual patient, and the evidence comes from studying people under real-world conditions. When you meet a study question, start by naming the exposure, the outcome and the population it concerns, and ask whether the exposure could be changed: epidemiologists give priority to modifiable causes because those are the ones an intervention can target.
- 1.2 Ideas about what causes disease have changed a great deal over the centuries. The Hippocratic tradition and later miasma theory looked to the environment (air, water, place and the "bad air" of decay), and although miasma theory was wrong about the mechanism, the sanitary reforms it prompted still reduced infection. Germ theory then brought a one-agent, one-disease logic that led to major successes such as immunisation and specific treatment, but by the mid-1900s single agents could no longer explain rising chronic disease, and studies such as Framingham and the 1950s work on smoking and lung cancer moved the field toward multifactorial models that combine biological, behavioural, social and environmental causes. Subsection 1.2 names the tension that runs through this history, between explaining disease through mechanisms inside individuals and explaining it through populations and their environments, and both views are needed. When a question challenges whether epidemiology can find causes, use the modern view: almost every outcome has several causes and a single cause can have several effects, so the lack of one identifiable agent does not mean a disease has no identifiable causes.
- 1.3 John Snow's cholera investigation in the mid-1800s is the classic example of population reasoning getting ahead of laboratory science. By looking at where cases occurred, running a series of observational studies and comparing households supplied by two different water companies (a natural experiment), he concluded that cholera spread through contaminated water about 30 years before Koch isolated Vibrio cholerae. The point to carry away is that you do not need to know the causal agent, or its biological mechanism, to prevent disease: acting on the source of exposure was enough. Goldberger's work on pellagra makes the same point, since dietary reform prevented the disease before niacin was identified. When a question asks what Snow showed, answer in terms of prevention: careful observation of who becomes ill, and where, can identify a cause and justify action before the agent is known.
1. A family doctor sees a child having an asthma attack and decides which inhaler to prescribe. A regional epidemiologist reviewing records from the same clinic notices that asthma visits are more common among children who live within 200 metres of a highway. Which question belongs to the epidemiologist rather than to the doctor?
2. A student is sorting four explanations that were offered, in different eras, for why communities suffered outbreaks of fever: (i) the air, water and place where people lived; (ii) foul-smelling air given off by rotting refuse; (iii) a specific microorganism for each disease; (iv) a web of interacting biological, behavioural and social factors. In what order did these ideas become dominant?
3. In 1854, John Snow traced a cholera outbreak in London to the Broad Street water pump and compared cholera deaths in households supplied by two different water companies, about 30 years before the organism Vibrio cholerae was isolated. A colleague argues: 'Public-health action against a disease should wait until laboratory scientists have identified the organism that causes it.' How does Snow's work bear on this argument?
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Scientific Inference & Key Research Components
⏱ Estimated reading time: 12 minutes
Overview
Section 1 traced the history of causal thinking. This section moves from history to logic and asks how epidemiologists reason from observed data to claims about cause and effect. It begins with the forms of reasoning that sit underneath every study design in this course, inductive, deductive and Bayesian, and then maps that reasoning onto the components of an epidemiologic study. It closes with the directed acyclic graph (DAG), the formal tool for writing down causal assumptions before any data are analysed: how to read one, how to use it to choose what to adjust for, and how it differs from mediation analysis.
Learning Objectives
- 2.1 Distinguish inductive from deductive reasoning and describe Popper's refutationism.
- 2.2 Explain how Bayesian thinking and scientific consensus combine prior knowledge with new evidence.
- 2.3 Describe the components of an epidemiologic study, from the source population to causal inference, and name selection bias and confounding as threats along that path.
- 3.1 Read a DAG: identify the exposure and the outcome, and recognise the three building blocks, a chain (mediator), a fork (confounder), and a collider.
- 3.2 Choose the variables to adjust for to estimate a total effect, and explain why conditioning on a collider, including restricting the sample, creates selection bias.
- 3.3 Explain how DAG-based reasoning differs from quantitative mediation analysis such as the Baron and Kenny approach.
2.1 Inductive and Deductive Reasoning
Epidemiology relies mainly on observational studies, because ethical concerns, practical limits and the complexity of real-world exposures mean that most health problems cannot be studied under controlled laboratory conditions. When researchers cannot assign the exposure themselves, the quality of their reasoning carries much of the weight, and two forms of reasoning do that work.
Inductive reasoning moves from repeated specific observations to a general conclusion, as when Edward Jenner generalised from milkmaids who had caught cowpox and did not develop smallpox. It is powerful for discovery, but however often an association is repeated, it remains consistent with causation without proving it. The reason is that each new observation adds to the pile of examples without ruling out other explanations: something else shared by the milkmaids could, in principle, have protected them, and seeing more protected milkmaids would not tell us otherwise.
Deductive reasoning runs in the opposite direction, from a general hypothesis to a specific prediction that can be tested against data. If cowpox protects against smallpox, for instance, then people deliberately given cowpox should resist smallpox when they are later exposed, and that prediction can be checked. Karl Popper's refutationism adds that scientists should try to disprove a hypothesis rather than to confirm it. By this we mean that a study is most informative when it sets up a fair chance for the hypothesis to fail: no number of confirming results can prove a general claim, but a single well-conducted test that contradicts it shows that something is wrong. This is why statistical analyses are framed around a null hypothesis of no association that the study then tries to reject.
The three tabs below give a fuller account of each form of reasoning and the thinkers behind it (Bacon, Mill, Hume, Popper), and the third tab adds Bayesian thinking, which the next subsection develops. Open each tab in turn and watch for the unifying point: no single mode of reasoning gives certainty, and epidemiologic claims always rest on a combination of observation, hypothesis testing and consensus.
Inductive Reasoning
Inductive reasoning involves making generalized inferences about causation based on repeated observations. You observe specific instances and draw broader conclusions.
Francis Bacon (1620) first presented inductive reasoning as a method of making generalizations from careful observations. Classic examples include Edward Jenner's observation that milkmaids who developed cowpox didn't get smallpox, which led to the development of the smallpox vaccine. John Stuart Mill's canons (1843) formalized rules for inductive inference and helped shape our concepts of necessary and sufficient causes.
However, as David Hume noted, inductive reasoning has no logical force; we cannot perceive a causal connection, only a series of events. Repeated observations may be consistent with causation but do not prove it.
Deductive Reasoning
Deductive reasoning involves inferring that a general "law of nature" exists and testing specific hypotheses against observations to prove or refute them. This approach is closely linked to refutationism, attributed to Karl Popper.
Popper argued that scientists should collect data to attempt to disprove a hypothesis rather than to prove it. Only by disproving hypotheses can we make scientific progress. This is why statistical analyses typically form hypotheses in the null (no association) and then attempt to refute them.
The key benefit: it helps narrow the scope of studies. We carefully review what is known and formulate a few specific, testable hypotheses rather than casting a wide net with hundreds of variables.
Bayesian Thinking & Scientific Consensus
Thomas Bayes (1764) noted that all inference is based on the validity of our premises and that no inference can be known with certainty. The information we have before making observations influences our interpretation of those observations. This gave rise to Bayesian analysis, which formally incorporates prior knowledge and updates it with new data.
Thomas Kuhn reminded us that although a single observation can disprove a hypothesis, the observation might be anomalous. Scientific communities therefore rely on consensus, and on paradigm shifts, when weighing the usefulness of theories, even if they cannot prove absolute truth.
To classify an example, ask which way the reasoning runs: from many observations toward a rule (inductive), or from a stated hypothesis toward a test (deductive). Because neither delivers certainty on its own, a further question arises: how far should a single new study change what researchers already believe?
2.2 Prior Knowledge, Bayesian Thinking and Scientific Consensus
Bayesian thinking, introduced in the third tab, answers that question by treating every inference as conditional on what was known before. Rather than asking whether a new finding settles the matter, it asks how far the finding should shift existing belief. By this we mean that the starting point (the prior) and the new evidence are weighed together, and the conclusion (the posterior) lands somewhere between them. For example, if dozens of large studies have found that a vaccine is safe and one small study reports a possible harm, the Bayesian reading is that confidence in the vaccine's safety should fall a little, not collapse, because the new result is weighed against a large body of earlier evidence. If, instead, a question has barely been studied, the same small study would move belief much further, because there is little prior evidence to weigh it against. This weighing of new results against accumulated evidence is also the logic of the systematic reviews and meta-analyses you will use throughout this course. Kuhn's point about consensus adds a social check: because a single contradictory observation may be anomalous, scientific communities weigh new findings against the existing body of evidence and change their views over time, occasionally through a paradigm shift. In practice, a surprising result from one study is read in the light of everything already known, and it is a reason to seek replication rather than to discard either the new study or the earlier evidence. Epidemiologic claims therefore rest on a combination of observation, hypothesis testing and consensus, and the next subsection shows where these forms of reasoning enter an actual study.
2.3 The Components of an Epidemiologic Study
The rationale for epidemiologic research is to identify causal associations between exposures, which are often potential risk factors, and outcomes, which are often diseases, so that causal inferences about the source population can support policy and prevention programmes. Every study pursues that goal along the same path, shown in Figure 1.1. Each box marks a step where a study can go wrong: how the sample is drawn from the source population, how exposures and outcomes are measured, and how confounding is handled.
Figure 1.1. Key components of epidemiologic research. Research starts from a source population, samples a study group, measures exposures and outcomes, accounts for extraneous variables (confounders and biases), and ultimately draws causal inferences.
The figure also shows where the forms of reasoning in 2.1 and 2.2 enter. The study begins from hypotheses deduced from prior knowledge, it gathers observations from a study group, and it ends with an inference that has to be judged against the wider body of evidence. Two threats lie along the path. Selection bias threatens the sampling step, because the way people come to be in the study group can make the group unrepresentative of the source population. Confounding threatens the comparison, because extraneous variables linked to both the exposure and the outcome can create or hide an association. When you read a study description, trace it along this path and ask what could go wrong at each step: a problem with who got into the study points to selection bias, and a third variable tied to both exposure and outcome points to confounding.
Figure 1.1 is informal, since its boxes and arrows do not commit to a precise causal meaning. The rest of this section introduces a formal tool for stating the causal assumptions that link the exposure, the outcome and the extraneous variables.
3.1 Reading a Directed Acyclic Graph
A directed acyclic graph (DAG) is the formal version of the picture in Figure 1.1 (Pearl, 1995; Greenland & Brumback, 2002). The name describes its three features. It is a graph because it is made of nodes, which are variables, connected by lines. It is directed because each line is an arrow pointing one way, from a cause to its effect. And it is acyclic because it contains no cycles: if you follow the arrows from any variable, you can never arrive back where you started, so no variable can cause itself even by a long route. Each arrow is a claim that one variable directly affects another. A missing arrow is just as much a claim, since it asserts that there is no direct effect. For example, leaving out an arrow from age to an exposure says that age has no direct influence on who becomes exposed, and if that is wrong, everything the diagram implies for the analysis may be wrong too. Epidemiologists use DAGs to write down their assumptions about how the world works before they touch the data, and then to read off what those assumptions imply for the analysis.
Reading a DAG starts with naming the exposure (X) and the outcome (Y). Every other variable is then classified by the structure it forms with them, and every DAG, however large, is built from three such structures, shown in the cards below (click a card for a fuller explanation). In a chain (X → M → Y), M is a mediator through which part of the effect travels: X changes M, and the change in M then changes Y. For example, exercise may lower blood pressure, and lower blood pressure in turn lowers the risk of stroke. In a fork (X ← C → Y), C is a confounder because it causes both the exposure and the outcome. Because C pushes on both, X and Y tend to move together even if X has no effect on Y at all; older age, for instance, makes people both more likely to take certain medicines and more likely to die. In a collider (X → Z ← Y), two arrowheads meet at Z, so Z is caused by both the exposure and the outcome. Unlike a fork, a collider does not by itself make X and Y appear related, because nothing flows outward from Z to either of them. The difficulty arises only if the analysis conditions on Z, which the cards and the next subsection explain.
Not every variable is a confounder, a mediator or a collider. A variable that causes only the outcome, with an arrow into Y and none into X, forms none of the three structures between X and Y, so it is classified as none of these.
The arrows themselves come from subject-matter knowledge of the system, not from p-values, so drawing a DAG is a substantive exercise rather than a statistical one. A workable recipe follows.
- Name the exposure (X) and outcome (Y), and put them on the page with the exposure on the left.
- List every other variable that could plausibly affect either X or Y, whether demographic, biological, social or environmental. Include unmeasured variables, drawn with dashed nodes, because they belong in the diagram even when you cannot put numbers on them.
- Draw an arrow from each variable to every variable it directly causes. Be strict about "direct": if A affects B only through C, draw A → C and C → B, not A → B.
- Check for cycles. If A causes B and B causes A, add a time index or break the loop with intermediate variables, because DAGs forbid feedback loops.
- Read off the implications for adjustment, which is the subject of 3.2.
Once every variable has been classified, the diagram can be used to decide which variables belong in the analysis.
3.2 Choosing What to Adjust For
The adjustment set for the total effect of X on Y follows from the classification in 3.1. A back-door path is a non-causal path from X to Y that begins with an arrow pointing into X, such as X ← C → Y. It is called a back door because it leaves X through the "back", against the direction of X's own effect, and reaches Y without passing through any effect of X. Association can flow along such a path, so if it is left open the comparison of exposed and unexposed people mixes the true effect of X with the influence of C. Every back-door path that does not pass through a collider must therefore be blocked by adjusting for a variable on it, which is why confounders are adjusted for.
Mediators and colliders are treated differently. Mediators are left alone, because adjusting for a mediator removes part of the very effect being estimated (over-adjustment). If exercise lowers stroke risk partly by lowering blood pressure, then comparing only people with the same blood pressure hides that part of the benefit. Colliders are also left alone, because a collider blocks the path it sits on until it is conditioned on, at which point it opens a non-causal path and creates a spurious association. The reason is that once we look only at people with a given value of the collider, knowing one of its causes tells us something about the other. For example, if a hospital admits people who have either a serious injury or a serious infection, then among admitted patients, someone without an injury is likely to have an infection, so the two conditions appear negatively related inside the hospital even if they are unrelated in the population. Restricting the sample to one level of a collider, for example studying only clinic visitors or only hospital patients, is the same as conditioning on it, so it also creates selection bias. A variable classified as none of these lies on no back-door path; adjusting for it introduces no bias and may improve precision, but it is not needed to remove confounding.
These rules show what a DAG contributes to an analysis. It identifies the confounders, since anything on a back-door path is a candidate for adjustment and anything off one is not, however statistically "significant" it appears. It flags the mediators and colliders that must not be adjusted for. It makes the assumptions open to criticism, because a reviewer can dispute a specific arrow in a way they cannot dispute a regression equation. Finally, it supports a transparent estimand, such as "the total effect of X on Y, adjusting for the back-door set {C1, C2}". Worked Example 1.1 applies the reading routine from 3.1 and these adjustment rules, one variable at a time, to a diagram that contains all four kinds of variable.
Worked Example 1.1: Classifying the Variables in a DAG
A health authority asks whether working night shifts (X) increases the risk of a workplace injury (Y) among hospital and warehouse employees. The team draws a DAG with these arrows, each based on subject-matter knowledge:
- Job sector → Night shifts and Job sector → Injury (warehouse jobs involve more night work and more physical hazards).
- Night shifts → Fatigue → Injury (night work causes fatigue, and fatigue causes injuries).
- Icy weather → Injury (slips on the way into work; weather does not decide who works nights).
- Night shifts → Clinic visit ← Injury (night workers are invited to the occupational-health clinic for routine checks, and injured workers go there for treatment).
Step 1, exposure and outcome. The exposure is night-shift work and the outcome is workplace injury.
Step 2, classify each variable and name its structure.
- Job sector is a confounder: it forms a fork, Night shifts ← Job sector → Injury, because it causes both the exposure and the outcome.
- Fatigue is a mediator: it lies on a chain, Night shifts → Fatigue → Injury, through which part of the effect travels.
- Icy weather is none of these: it causes the outcome only, has no arrow into the exposure, and lies on no back-door path.
- Clinic visit is a collider: two arrowheads meet at it, Night shifts → Clinic visit ← Injury.
Step 3, the adjustment set for the total effect. Adjust for job sector, the only variable on a back-door path. Do not adjust for fatigue (a mediator), because that would remove part of the effect being estimated, and do not adjust for clinic visit (a collider). Adding icy weather to the set, {Job sector, Icy weather}, is also acceptable because it introduces no bias.
Step 4, what restricting the sample would do. Suppose a colleague proposes to study only the workers who visited the clinic, because their records are easiest to obtain. Restricting the sample to one level of a collider is the same as conditioning on it: it opens the non-causal path Night shifts → Clinic visit ← Injury and creates selection bias. Among clinic visitors, day workers were mostly there because they were injured, while many night workers were there for a routine check, so injury is over-represented among the day workers in the sample. The estimated effect of night shifts would be distorted, here pulled toward no effect.
Reading a DAG is a fixed routine: name the exposure and the outcome, classify every other variable by the structure it forms with them, adjust for the variables that block back-door paths, and leave mediators and colliders alone, including when choosing who enters the sample.
The worked example left fatigue, the mediator, out of the adjustment set because the target was the total effect. A different question is how much of the effect of night shifts runs through fatigue, and that question belongs to mediation analysis.
3.3 DAGs and Mediation Analysis
A DAG tells you that a variable lies on the pathway from exposure to outcome. Mediation analysis puts numbers on how much of the exposure's effect runs through that mediator and how much runs around it. Given a chain X → M → Y, in which X may also affect Y directly, it asks how much of the total effect of X on Y is the indirect effect through M and how much is the direct effect that does not pass through M, so that the total effect equals the direct effect plus the indirect effect.
The causal-steps procedure of Baron and Kenny (1986) is the approach most students meet first. It runs three regressions and checks four conditions.
- Step 1. Total effect. Regress Y on X. The slope (call it c) must be significant. This is the total X → Y effect.
- Step 2. X predicts M. Regress M on X. The slope (a) must be significant. If X does not move M, M cannot be a mediator.
- Step 3. M predicts Y, controlling for X. Regress Y on both X and M. The coefficient on M (call it b) must be significant.
- Step 4. Compare c to c′. The X coefficient in Step 3 (c′) is the direct effect. If c′ is much smaller than c, the gap (c − c′, equivalently a×b) is the indirect effect through M. If c′ is essentially zero, the mediation is “complete”; otherwise it is “partial.”
The procedure is intuitive but limited. It assumes linear models, no interaction between the exposure and the mediator, and no unmeasured confounding of the relationship between M and Y. Each assumption matters for a concrete reason. Linearity means the method is built for continuous outcomes, so it does not carry over neatly to an outcome such as ill or not ill. No interaction means the effect of M on Y is assumed to be the same for exposed and unexposed people, which may not hold if, say, fatigue is more dangerous on a night shift than on a day shift. And because the step 3 regression compares people with different levels of M, any unmeasured factor that affects both M and Y will distort b, and with it the estimated indirect effect.
Two modern alternatives address these limits. The first concerns uncertainty. The Sobel z-test, the traditional significance test for the indirect effect a×b, assumes that this product follows a normal distribution, which it often does not, so its results are unreliable. Preacher and Hayes therefore recommended bootstrap confidence intervals, which resample the data many times and use the spread of the resulting a×b values to describe the uncertainty directly. The second concerns the definition of the effects themselves. Counterfactual or causal mediation methods (Imai, Pearl, VanderWeele) define natural direct and indirect effects as comparisons of potential outcomes, an idea developed in Section 4, rather than as regression coefficients. Because the definitions do not depend on a particular model, they do not require linearity, which allows binary outcomes and exposure-mediator interactions.
Because both tools involve arrows and pathways, DAGs and mediation analysis are easy to conflate, but they answer different questions. A DAG is qualitative: it encodes which variables cause which others and lets you read off what should be adjusted for, without fitting a model or estimating an effect. Mediation analysis is quantitative: it estimates the size of the direct and indirect effects, given a model that has already been specified. The two work in sequence. The DAG shows whether mediation analysis is appropriate, by checking that M really lies on the pathway and whether back-door paths between M and Y need adjustment, and it identifies the variables to put in the regressions; the mediation analysis then says how much of the effect runs through the mediator. A Baron and Kenny analysis run without that DAG-level thinking can give precise numbers for a misspecified pathway, while a DAG without follow-up estimation gives the structure but not the magnitude. Every credible mediation analysis therefore sits on top of a DAG, although not every DAG calls for a mediation analysis.
This section has set out the forms of reasoning behind epidemiologic inference, the components of a study, and the use of DAGs and mediation analysis to represent causal pathways and estimate effects along them. The key takeaways below summarise these points.
Key Takeaways
- 2.1 Inductive and deductive reasoning run in opposite directions. Inductive reasoning moves from specific observations to a general conclusion, as when Jenner noticed that milkmaids who caught cowpox did not get smallpox; it is useful for discovery, but, as Hume pointed out, repeated association never proves causation. Deductive reasoning moves the other way, from a general hypothesis to a specific prediction that can be tested against data. Popper's refutationism adds that science advances by trying to disprove hypotheses rather than by piling up confirmations, which is why statistical analyses are set up around a null hypothesis of no association that the study then tries to refute. To classify an example, ask which way the reasoning runs: from many observations toward a rule (inductive), or from a stated hypothesis toward a test (deductive).
- 2.2 Bayesian thinking starts from the idea that no inference is certain and that what we already know shapes how we read new data. Bayesian analysis makes this formal: it begins with prior knowledge and updates it with the results of a new study, so the question becomes how far a new finding should shift what was already believed. Kuhn added that although one observation can disprove a hypothesis, that observation might be anomalous, so scientific communities weigh new findings against existing theory and reach consensus over time, occasionally through a paradigm shift. In practice, never read a single study in isolation: when a question describes a surprising result, say how it fits with the existing body of evidence and why one study, on its own, rarely settles a causal question.
- 2.3 Every epidemiologic study follows the same path, shown in Figure 1.1. It starts from a source population, samples a study group, measures exposures and outcomes, accounts for extraneous variables, and then draws causal inferences back to the source population, which is where policy and prevention will apply. Two threats sit along that path: selection bias threatens the sampling step, through the way people come to be in the study group, and confounding threatens the comparison, through extraneous variables linked to both the exposure and the outcome. When you read a study description, trace it along this path and ask what could go wrong at each step; a problem with who got into the study points to selection bias, and a third variable tied to both exposure and outcome points to confounding.
- 3.1 A DAG (directed acyclic graph) is a way of writing down your causal assumptions as a picture. Each node is a variable, each arrow is a claim that one variable directly affects another, a missing arrow is a claim of no direct effect, and no path of arrows may loop back on itself. To read one, first name the exposure and the outcome, then look at how every other variable connects to them: a fork (X ← C → Y) makes C a confounder because it causes both, a chain (X → M → Y) makes M a mediator because part of the effect travels through it, and a collider (X → Z ← Y) is a variable that two arrowheads point into. Not every variable fits one of these; a variable that causes only the outcome, like icy weather in Worked Example 1.1, is none of these. On an exam, classify the variables one at a time and name the structure that supports each answer (for example, "job sector is a confounder because it forms the fork Night shifts ← Job sector → Injury"), because the structure is what justifies the classification.
- 3.2 Once each variable is classified, the adjustment set for the total effect follows a simple rule: adjust for the confounders that block back-door paths, and leave mediators and colliders alone. Adjusting for a mediator removes part of the very effect you are trying to estimate (over-adjustment), and adjusting for a collider opens a non-causal path between the exposure and the outcome that was blocked before. Restricting the sample to one level of a collider, such as studying only clinic visitors or only hospital patients, is the same as conditioning on it, so it also creates selection bias. Adding a variable that causes only the outcome does no harm, which is why {Job sector, Icy weather} is as acceptable as {Job sector} in Worked Example 1.1. When a question proposes analysing a convenient subgroup, check whether membership of that subgroup is affected by both the exposure and the outcome; if it is, say that the restriction conditions on a collider, opens a non-causal path and distorts the estimate.
- 3.3 DAGs and mediation analysis both involve arrows and pathways, but they answer different questions. A DAG is qualitative: it states which variables cause which, and from it you read off what to adjust for, without fitting a model or estimating an effect. Mediation analysis is quantitative: given a chain X → M → Y, it estimates how much of the total effect is indirect (through M) and how much is direct, so that the total effect equals the direct plus the indirect effect. In the Baron and Kenny approach you regress Y on X to get the total effect c, regress M on X to get a, and regress Y on both X and M to get b and the direct effect c′; the indirect effect is c − c′, equivalently a×b. Remember that every credible mediation analysis sits on top of a DAG: draw the diagram first to check that M really lies on the pathway and whether back-door paths between M and Y need adjustment, because precise numbers for a misspecified pathway are still wrong.
1. Over several winters, a school nurse notices that pupils who walk to school seem to miss fewer days with colds, and she concludes that walking to school protects against colds. A research team then states the hypothesis 'walking to school has no effect on colds', works out what they should observe if it were true, and designs a study to try to reject it. Which statement describes the two approaches correctly?
2. Fifteen large, well-conducted studies over twenty years have found no link between a common food additive and childhood eczema. A new study of 90 children reports that children who ate the additive were twice as likely to develop eczema. Which response best reflects Bayesian thinking and the role of scientific consensus?
3. Researchers want to know whether regular physical activity reduces depression among all adults in a health region (the source population). They recruit their study group through advertisements posted in fitness centres. They also know that adults with a chronic illness tend to be less active and are more often depressed. Which threats do these two facts pose, in that order?
4. A study asks whether daily vaping (the exposure) increases asthma attacks (the outcome) among teenagers. The team's DAG contains these arrows: Peer smoking → Vaping; Peer smoking → Asthma attacks; Vaping → Airway inflammation → Asthma attacks; Pollen season → Asthma attacks. How should peer smoking, airway inflammation and pollen season be classified?
5. A DAG for the question 'Do long working hours (X) cause high blood pressure (Y)?' contains these arrows: Age → X and Age → Y; Job type → X and Job type → Y; X → Stress → Y; and X → Wellness-programme enrolment ← Y (employers enrol staff who work long hours, and doctors refer patients with high blood pressure). Which set of variables should be adjusted for to estimate the total effect of X on Y?
6. Researchers ask whether regular physical activity reduces depression among university students. To save time, a colleague proposes recruiting only students who visit the campus health clinic. Active students often visit the clinic with sports injuries, and students with depression often visit it for counselling. What would this restriction do to the estimate?
7. A team's DAG shows that a school breakfast programme (X) raises mathematics test scores (Y) both directly and through better attention in class (M). A Baron and Kenny analysis then estimates a total effect of c = 10 points and a direct effect of c′ = 6 points. Which statement is correct?
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Seeking Causes & Models of Causation
⏱ Estimated reading time: 15 minutes
Overview
Section 2 supplied the inferential machinery and the vocabulary of directed acyclic graphs. This section asks what we actually mean when we draw an arrow on a DAG and call it a “causal effect.” It begins with a working definition of a cause, then develops the component-cause model, with its necessary, sufficient and component causes, and uses it to explain why the same cause can show different strengths of association in different populations. It then describes the causal-web model and the population attributable fraction, a quantity that turns the abstract notion of cause into a number a public-health planner can use, and it closes with the Bradford Hill viewpoints, the classic aids for judging whether an observed association is likely to be causal.
Learning Objectives
- 4.1 Define a cause in epidemiology as any factor that changes the frequency or severity of an outcome.
- 4.2 Define necessary, sufficient, and component causes in the component-cause model, and classify the causes of a described disease using these terms.
- 4.3 Explain how the prevalence of causal complements changes the strength of association, so that the same exposure can show different risk ratios in different populations.
- 4.4 Describe the causal-web model, distinguish direct from indirect causes, and explain why population attributable fractions can sum to more than 100 per cent.
- 5.1 Use the nine Bradford Hill viewpoints, with temporality as the only strict requirement, to argue whether an observed association is likely to be causal.
4.1 What Counts as a Cause
For practical purposes in epidemiology, a cause is any factor that produces a change in the severity or frequency of an outcome. The definition is deliberately practical: a cause does not have to act every time, or on its own, only to shift how often or how severely the outcome occurs. Some causes operate at the biological level within individuals (such as a specific microorganism), while others operate at the group or population level (such as lifestyle, nutrition, or weather).
Epidemiology deals with groups of individuals because the methods for determining causality require it. Because a cause is defined as something that changes how often or how severely an outcome occurs, its effect can only be seen by counting outcomes across many people. A single smoker who develops lung cancer, or a single smoker who does not, says little about whether smoking is a cause; it is the higher frequency of lung cancer among many smokers, compared with many non-smokers, that reveals the effect. Researchers take a holistic approach, striving to study and measure every suspected causal factor for the outcome of interest, while recognising that not every factor can be captured in a single study. Within that range, epidemiologists prefer to identify causal factors that can be manipulated to prevent disease, although some non-manipulable factors (like genetic predisposition) may also be important for understanding disease patterns in populations. When you decide whether a factor counts as a cause, test it against this definition rather than asking whether it is necessary or sufficient by itself, terms that the next subsection makes precise.
Most diseases have several causes acting together, and the next subsection describes a model of how they combine.
4.2 Necessary, Sufficient and Component Causes
The component-cause model, developed by Rothman (1976) and elaborated by Rothman & Greenland (2005), distinguishes three kinds of cause: necessary, sufficient and component. Their definitions build on one another, so expand the three panels below in order and make sure you can state each definition in your own words before reading on.
A necessary cause is one without which the disease cannot occur. The factor will always be present if the disease occurs. For example, Mycobacterium tuberculosis is a necessary cause of tuberculosis, since you cannot develop TB without the bacterium being present.
A sufficient cause is a set of conditions that, when present, will invariably produce the disease. By this we mean a complete recipe: once every ingredient is in place, the disease follows, and nothing more is needed. In practice, very few single exposures are sufficient on their own. Exposure to the tuberculosis bacterium, for example, does not make everyone ill; disease usually follows only when the bacterium is joined by other conditions, such as a weakened immune system. Instead, different groupings of factors combine to form sufficient causes, and a disease may have several such groupings, each of which can produce it.
A component cause is one of a number of factors that, in combination, constitutes a sufficient cause. In terms of the recipe, it is a single ingredient: necessary for that particular recipe to work, but unable to produce the disease without the others. The factors might be present at the same time or follow one another in a temporal chain; for example, a poor diet might weaken a person's immunity months before they meet an infectious agent. Because removing any one ingredient stops that recipe from being completed, every component cause is a possible target for prevention. When there are a number of causal chains with one or more factors in common, we can conceptualize the web of causal chains as a causal web.
The three terms are not mutually exclusive, and one cause can fit more than one of them. Consider salmonellosis after eating chicken. The bacterium Salmonella is a necessary cause of salmonellosis, because the disease cannot occur without it, and it is also a component of every sufficient cause of the disease. Eating contaminated chicken is a component cause: it completes a sufficient cause only together with its causal complements, such as cooking that is too light to kill the bacteria, a large enough dose, and a susceptible person. It is not necessary, because people can be infected through other foods, and it is not sufficient on its own, because thoroughly cooked contaminated chicken causes no illness. A study that finds a risk ratio close to 1 for contaminated chicken in a kitchen that cooks every piece thoroughly shows the same point: when a complement (undercooking) is missing, the component (the contaminated food) no longer completes a sufficient cause.
A disease can also have several different sufficient causes, and then no single factor need be necessary. Consider four risk factors for childhood respiratory disease (CRD): the bacterium Streptococcus pneumoniae (STREP), a virus (RSV), environmental stressors like cold weather, and other bacteria like Mycoplasma pneumoniae (MP). Different two-factor combinations of these can form sufficient causes, and Table 1.1 sets out four of them.
Table 1.1. Component causes of childhood respiratory disease (CRD) and the four two-factor sufficient causes they form.
| Component Causes | Sufficient Cause I | Sufficient Cause II | Sufficient Cause III | Sufficient Cause IV |
|---|---|---|---|---|
| STREP | + | + | ||
| RSV | + | + | ||
| Stressors | + | + | + | |
| Other organism (MP) | + |
Table 1.1 shows that no single factor is a necessary cause of CRD, because none appears in every sufficient cause. STREP is a component of 2 of the 4 sufficient causes, so it produces disease only when RSV or stressors complete the set, and a child exposed to any complete combination will develop CRD. To classify a cause, then, ask two questions: could the disease occur without it (if not, it is necessary), and would it produce the disease on its own (almost never, which is why most exposures are components)?
Because a component cause acts only together with the other factors in its sufficient cause, the observed strength of association between an exposure like STREP and CRD can change even though the underlying causal mechanism has not changed, which is the subject of the next subsection.
4.3 Causal Complements and the Strength of Association
A critical insight from the component-cause model is that the prevalence of causal complements, the other factors needed to complete a sufficient cause, directly affects the strength of association we observe between an exposure and outcome. Even when the causal mechanism stays the same, changes in the distribution of co-factors in the population can make the association appear stronger or weaker. To see why, return to the contaminated chicken. In a community where most cooks undercook chicken, contaminated chicken will usually find its complement, and people who eat it will fall ill far more often than people who do not, giving a large risk ratio. In a community where nearly everyone cooks chicken thoroughly, the same contaminated chicken rarely completes a sufficient cause, so eaters and non-eaters fall ill at similar rates and the risk ratio is close to 1. The bacterium and the biology are identical in both places; only the prevalence of the complement differs. This is one of the most frequently misread points in causal reasoning, because it is tempting to treat a risk ratio as a fixed property of the exposure when it is partly a property of the population studied.
Strength of Association Is Population-Specific
The same causal mechanism can produce different risk ratios in different populations, because the risk ratio depends on how common the causal complements, and the other sufficient causes, are in each population. When two well-conducted studies of the same exposure report different risk ratios, do not conclude that one of them must be wrong or that the exposure is more harmful in one place; ask whether the populations differ in the prevalence of the other factors needed to complete a sufficient cause.
Worked Example 1.2 puts numbers on this for STREP, using the sufficient causes in Table 1.1 and comparing two populations that differ only in how common RSV is. As you read it, watch what happens to the risk in the STREP-unexposed group.
Worked Example 1.2: How Co-Factor Prevalence Matters
Imagine STREP requires RSV or Stressors as a co-factor to cause CRD. In Population A, where RSV prevalence is 30%, the risk ratio for STREP is 4.83. In Population B, where RSV prevalence rises to 70%, the risk ratio drops to 2.93, even though the causal relationship between STREP and CRD has not changed at all.
Here is the intuition for why the ratio shrinks. When RSV becomes more common, more children develop CRD through pathways that do not involve STREP at all (for example RSV together with stressors), which raises the disease risk in the STREP-unexposed group. Because the risk ratio divides the risk in the exposed by the risk in the unexposed, a larger unexposed risk pulls the ratio down toward 1, even though STREP itself is doing exactly what it always did.
The difference is due entirely to the change in the frequency of the co-factor RSV. This is why strength of association is not a fixed measure and is considered "population specific."
The example showed that a more common co-factor raises the risk in the unexposed and pulls the risk ratio toward 1, and the same reasoning explains the risk ratio close to 1 for contaminated chicken in a kitchen that cooks every piece thoroughly. The component-cause model explains the abstract logic of multicausality, and the next subsection turns to the causal-web model, the related diagrammatic tool for thinking about how those component causes connect in the real world and where you can intervene.
4.4 Causal Webs and the Proportion of Disease Explained
An alternative way to visualise how multiple factors combine to cause disease is the causal web, consisting of interconnected direct and indirect causal chains. The central distinction is between causes that act on the outcome with nothing in between and causes that act through other variables. Open each of the three tabs below: the first two define direct and indirect causes, with an example from childhood respiratory disease, and the third sets out what the web implies for disease control.
Direct (Proximal) Causes
A direct cause has no known intervening variable between it and the disease. Diagrammatically, the exposure is adjacent to the outcome, joined to it by a single arrow. Examples often include specific microorganisms or toxins. The word "known" matters here: a cause looks direct only because no intervening step has yet been identified, and later research may reveal one. However, in disease control, direct causes are not necessarily more valuable than indirect ones; many large-scale control efforts work by manipulating indirect rather than direct causes. For example, the decline of tuberculosis in many countries began before effective drugs existed, partly because improvements in housing and nutrition reduced crowding and susceptibility, which act on the disease through other variables rather than on the bacterium itself.
Indirect Causes
An indirect cause is one whose effects on the outcome are mediated through one or more intervening variables. For example, Stressors (cold weather) may make a child susceptible to STREP, RSV, and MP, so Stressors act as an indirect cause of CRD. Removing stress could reduce CRD even though stress itself is not a direct cause.
Implications of the Causal Web
The causal-web model complements the component-cause model but is not equivalent. It shows that we can control disease by preventing the action of direct causes (e.g., vaccination against RSV) or by removing indirect causes (e.g., reducing environmental stressors). The diagram also reveals gaps in our knowledge: apparent direct connections might actually reflect unmeasured intervening factors.
To classify a cause in a web, look at its position: if nothing lies between it and the outcome it is direct, and if its effect passes through other variables it is indirect. Either kind can be a target for prevention, and direct causes are not automatically the more valuable ones.
The ideas of necessary and sufficient causes also let us estimate how much disease a given exposure explains. The population attributable fraction (AFp) is the proportion of disease in the population that is attributable to a given exposure, that is, the proportion of cases that would not occur if the exposure were removed, assuming the exposure is a cause. Levin (1953) showed that it can be calculated from two numbers, the prevalence of the exposure in the source population (pe) and the risk ratio for the exposure (RR), as shown in Equation 1.1.
AFp = pe(RR − 1) / [pe(RR − 1) + 1]
Equation 1.1. Levin's population attributable fraction.
To use Equation 1.1, multiply the prevalence of exposure by the risk ratio minus 1, then divide that result by itself plus 1. For example, if 30 per cent of a population is exposed (pe = 0.30) and the risk ratio is 3, the numerator is 0.30 × (3 − 1) = 0.60, the denominator is 0.60 + 1 = 1.60, and AFp = 0.60 ÷ 1.60 = 0.375. In words, about 37.5 per cent of the cases in this population would not occur if the exposure were removed, assuming the association is causal.
When fractions are calculated for several exposures, a result that surprises many students follows. Because each case is attributable to every component cause of the sufficient cause that produced it, and removing any one of those components would prevent that case, the AFp values for all factors can sum to more than 100%. Consider a child whose respiratory disease arose through Sufficient Cause I in Table 1.1, STREP together with RSV. Removing STREP would have prevented that case, and so would removing RSV, so the case is counted in the attributable fraction for STREP and again in the attributable fraction for RSV. When every case is counted once for each of its component causes, the fractions overlap, and their total can exceed 100%. This is not an error; it reflects the reality of multicausal disease, since fractions that added to exactly 100% would require every case to have only one cause.
The models so far describe how known causes combine; the final subsection asks how to judge whether an observed association reflects a cause at all.
5.1 Judging Causation with the Bradford Hill Viewpoints
Bradford Hill (1965) offered nine viewpoints for judging whether an observed association is likely to be causal. Interactive 1.1 presents them one card at a time as a game show; press Next to step through all nine, then use the list after it, which states in plain words the one question each viewpoint asks.
Flip through Bradford Hill's 9 viewpoints one card at a time. Next ▶ reveals each criterion.
An 11-scene game-show walkthrough of the Bradford Hill (1965) viewpoints: strength, consistency, specificity, temporality (the only hard rule), gradient, plausibility, coherence, experiment, and analogy, framed as a structured judgment rather than a checklist.
- Strength: is the association large (for example, a high risk ratio)? Strong associations are harder to explain away by bias alone.
- Consistency: has the association been seen by different investigators, in different places, with different methods?
- Specificity: is one exposure linked to one particular outcome, rather than to many?
- Temporality: did the exposure come before the outcome? This is the only viewpoint that must be satisfied, because a cause cannot follow its effect.
- Biological gradient (dose-response): does more exposure bring more disease?
- Plausibility: is there a believable biological or social mechanism?
- Coherence: does a causal interpretation fit what is already known about the natural history and biology of the disease?
- Experiment: does removing or reducing the exposure, by design or by circumstance, reduce the disease?
- Analogy: have similar exposures been shown to cause similar diseases?
The viewpoints are aids to judgement, not a checklist to score. Apart from temporality, a cause can fail any one of them, and a non-causal association can pass several. For example, smoking fails specificity, because it causes many diseases rather than one, yet it is unquestionably a cause of lung cancer. In the other direction, a strong and consistent association between carrying a lighter and lung cancer would pass strength and consistency without being causal, because both reflect smoking. Counting how many viewpoints are met therefore does not settle the question; what matters is how well the evidence for each one holds up. One of them, however, has a special status.
Temporality Comes First
Temporality is the only viewpoint that must be satisfied, because a cause cannot follow its effect. Check it first, and watch for designs that cannot show it, such as a one-time survey that measures the exposure and the outcome at the same moment. Meeting temporality is necessary but not sufficient: it does not on its own establish a cause.
To use the viewpoints in an answer, state a conclusion, apply temporality, and then support the conclusion with the viewpoints that the evidence actually speaks to, saying in each case what the evidence shows. Worked Example 1.3 applies this approach to a foodborne outbreak; watch how the timing of the first case, the peak and the last case, compared with the incubation period, does much of the work.
Worked Example 1.3: Applying the Viewpoints to an Outbreak
At a community barbecue held at noon on a Saturday, 200 people ate lunch. Over the next few days 45 became ill with diarrhea and fever, and stool cultures grew Salmonella. The illness began in 42 of the 120 people who ate the grilled chicken (35 per cent) and in 3 of the 80 who did not (about 4 per cent), a risk ratio of about 9. Salmonella usually causes illness 12 to 72 hours after exposure, with a range of about 6 hours to 6 days. The first case began on Saturday evening, the number of new cases peaked on Sunday afternoon, and the last case began on Tuesday morning. Is the outbreak consistent with a single exposure at the barbecue?
- Conclusion: yes, the pattern is consistent with a single point exposure at the barbecue lunch.
- Temporality: every case began after the lunch, so the exposure came before the illness, the one requirement that must be met.
- Coherence with the natural history: the first case began about 8 hours after the meal (within the shortest incubation), the peak came about a day later (within the usual 12 to 72 hours), and the last case began within about three days. Counting back one typical incubation period from the peak points to Saturday midday. The curve also has the shape expected of a point source: a steep rise, a single peak, and a fall within about one incubation period.
- Strength: people who ate the chicken were about nine times as likely to become ill as those who did not.
- Plausibility and specificity: Salmonella is a recognised cause of illness from undercooked poultry, and one organism produced one syndrome in a group that shared one meal.
The answer does not tick all nine viewpoints. It states a conclusion, applies temporality first, and then uses the viewpoints the data can speak to, here the timing against the incubation period, the strength of the association, and plausibility.
The same pattern carries over to any outbreak: check temporality, compare the first case, the peak and the last case with the incubation period, and then add the strength of the association and the plausibility of the mechanism.
Additional Context
The prevention paradox described here is background rather than an exam objective, but it follows from the population-level view of causes taken throughout this section. Even when a factor prevents a large share of disease (say a vaccine with a prevented fraction of 50%), the benefit at the individual level may appear modest. If disease prevalence was 6%, universal vaccination would reduce it to 3%. While 94% of the vaccinated population would not have gotten the disease anyway, the 3% reduction is still a major population-level achievement. However, half of those who would have gotten sick will still get the disease despite being vaccinated. This creates a paradox: the average person may not perceive the same benefit that population-level data show.
This section has defined cause, set out the component-cause and causal-web models, shown how they bear on the strength of association and the proportion of disease explained, and shown how to use the Bradford Hill viewpoints. The key takeaways below summarise these points before the final section turns to the counterfactual model.
Key Takeaways
- 4.1 In epidemiology, a cause is any factor that changes how often an outcome occurs or how severe it is. This is a deliberately practical definition: a cause does not have to act every time, or on its own, only to shift the frequency or severity of the outcome. Causes can operate within individuals (a specific microorganism) or at the group and population level (lifestyle, nutrition, weather), and they span biological, behavioural and social influences. Epidemiologists give priority to causes that can be manipulated, because those are the ones prevention can act on, although non-modifiable factors such as genetic predisposition still help explain disease patterns. When a question asks whether a factor counts as a cause, test it against this definition rather than asking whether it is necessary or sufficient by itself.
- 4.2 Rothman's component-cause model gives you three linked terms. A necessary cause is one without which the disease cannot occur (Mycobacterium tuberculosis for tuberculosis), a sufficient cause is a complete set of conditions that, when present together, invariably produces the disease, and a component cause is one of the factors that together make up a sufficient cause. The terms are not mutually exclusive: an infectious agent such as Salmonella is both a necessary cause and a component of every sufficient cause, while eating contaminated chicken is a component cause that completes a sufficient cause only together with complements such as undercooking, a large enough dose and a susceptible person. To classify a cause in a question, ask two things: could the disease occur without it (if not, it is necessary), and would it produce the disease on its own (almost never, which is why most exposures are components). A risk ratio near 1 in a setting where a complement is missing, such as a kitchen that cooks every piece thoroughly, is a clue that the exposure is a component that needs that complement, not a sign that it can never cause disease. Also remember that when a disease has several different sufficient causes, as childhood respiratory disease does in Table 1.1, no single factor need be necessary.
- 4.3 The strength of an association is not a fixed property of an exposure; it depends on the population. Because a component cause produces disease only alongside its causal complements, the risk ratio you observe for it changes when the prevalence of those complements changes, even though the biology is exactly the same. In Worked Example 1.2, the risk ratio for STREP falls from 4.83 when RSV prevalence is 30 per cent to 2.93 when it is 70 per cent, because more children in the STREP-unexposed group develop disease through pathways that do not involve STREP, which raises the risk in the denominator and pulls the ratio toward 1. So when two well-conducted studies of the same exposure report different risk ratios, do not conclude that one of them must be wrong; ask whether the populations differ in the prevalence of the other factors needed to complete a sufficient cause.
- 4.4 The causal-web model draws causes as interconnected chains leading to the outcome. A direct (proximal) cause has no known intervening variable between it and the disease, while an indirect cause acts through one or more intervening variables, as cold-weather stressors make children more susceptible to STREP, RSV and MP. Disease can be controlled at either level, and direct causes are not automatically more valuable: many large-scale control efforts work by removing an indirect cause, such as reducing environmental stressors. To classify a cause in a web, look at its position: if nothing lies between it and the outcome it is direct, and if its effect passes through other variables it is indirect. Finally, because each case is attributable to every component of the sufficient cause that produced it, the population attributable fractions (Levin's AFp) for all the risk factors of a disease can sum to more than 100 per cent; this is not an arithmetic error, because removing any one of those components would prevent the same case.
- 5.1 Bradford Hill's nine viewpoints (strength, consistency, specificity, temporality, biological gradient, plausibility, coherence, experiment and analogy) are questions that help you judge whether an association is likely to be causal. They are aids to judgement, not a checklist to score: apart from temporality, a real cause can fail any one of them, and a non-causal association can pass several. Temporality is the only strict requirement, because a cause cannot follow its effect, so check it first and watch for designs that cannot show it, such as a one-time survey that measures exposure and outcome at the same moment. Meeting temporality is necessary but not enough, so build the rest of the argument from the viewpoints the evidence actually speaks to. Follow the pattern of Worked Example 1.3: state your conclusion, apply temporality, then add two or three further viewpoints and say what the evidence shows for each; for an outbreak, compare the first case, the peak and the last case with the incubation period (coherence), and note the size of the risk ratio (strength) and whether the mechanism is plausible.
1. A city introduces a tax on sugary drinks. Over the next five years, tooth decay among its children falls, while a similar city without the tax sees no change. A colleague says, 'The tax cannot be a cause of the fall in tooth decay, because a cause has to be a biological agent acting inside the body.' What is wrong with the colleague's statement?
2. At a farm open house, visitors were offered samples of raw (unpasteurised) milk. Over the following two weeks, 24 visitors developed Campylobacter infection, and no cases were known among them before the event. Campylobacter usually causes illness 2 to 5 days after exposure, with a range of 1 to 10 days. The first case began 1 day after the open house, the number of new cases peaked 3 to 4 days after it, and the last case began 9 days after it. Which argument uses the Bradford Hill viewpoints correctly?
3. In an outbreak of listeriosis linked to one brand of soft cheese contaminated with Listeria monocytogenes, most of the people who became ill were pregnant women or adults over 65. Many healthy younger adults ate the same cheese and stayed well, and a few of the cases had eaten other contaminated foods instead. How should the bacterium and eating the contaminated cheese be classified?
4. A chemical used in local industry causes a skin condition only together with a particular genetic trait, which is equally common in Town A and Town B. The condition can also arise through a second sufficient cause that does not involve the chemical at all, and the components of that second cause are much more common in Town B. The biological mechanism is the same in both towns. The table shows the 10-year risk of the condition. Which statement is correct?
| Town | Risk among the exposed | Risk among the unexposed |
|---|---|---|
| A | 11.8 per cent | 2.0 per cent |
| B | 17.2 per cent | 8.0 per cent |
5. A causal web for lead poisoning in young children includes this sequence of links: Low household income → Living in older rental housing → Peeling lead-based paint → Child swallows paint chips and dust → Lead poisoning. Which statement is correct?
6. Suppose a regional report estimates the population attributable fraction (AFp) of a chronic disease for three exposures: physical inactivity 30 per cent, a low-fibre diet 45 per cent and obesity 35 per cent, which add up to 110 per cent. A journalist says the report must contain an error. How should you respond?
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The Counterfactual Concept
⏱ Estimated reading time: 12 minutes
Overview
Section 3 walked through classical models of causation: necessary and sufficient causes, the causal web, and the population attributable fraction. Those models are about the structure of causation. This final section is about the modern logic of causal inference, specifically the potential-outcomes framework, also called the counterfactual model. It first builds the framework: the counterfactual question, why individual effects cannot be observed, the average treatment effect that takes their place, and the exchangeability that randomisation provides. It then carries the framework into observational research: how confounding undermines exchangeability, how studies try to restore it, and how every analytic technique (propensity scores, regression, difference-in-differences, mediation) is a different way of approximating the same impossible quantity: what would have happened if the same person had not been exposed.
Learning Objectives
- 6.1 Define the potential-outcomes (counterfactual) model and state the counterfactual question for an exposed group.
- 6.2 Explain the fundamental problem of causal inference, namely why individual causal effects cannot be directly observed.
- 6.3 Describe how the average treatment effect (ATE), estimated by comparing groups, provides a group-level alternative, and name the comparison group that stands in for the counterfactual in a described study.
- 6.4 Define exchangeability and explain how randomised experiments create it.
- 7.1 Define a confounder, explain how it distorts a crude comparison, and explain why exchangeability is harder to assume in observational studies than in randomised trials.
- 7.2 Describe how observational studies address confounding through restriction, matching, stratification, and multivariable adjustment.
- 7.3 Recognise how counterfactual logic motivates the major analytic tools used in modern epidemiology, including propensity score matching, regression, difference-in-differences, and mediation analysis.
6.1 Potential Outcomes and the Counterfactual Question
The potential outcomes framework, also called the counterfactual model and sometimes the Neyman-Rubin causal model after the statisticians who formalized it (Rubin, 1974), is currently the most widely accepted conceptual basis for causal inference in epidemiology and across the modern health and social sciences. At its core, it asks a deceptively simple question: What would have happened to this same person if they had not been exposed?
For any individual i, the framework imagines two potential outcomes: Yi(1), the outcome we would observe if person i were exposed (or treated), and Yi(0), the outcome we would observe if that same person were unexposed (or untreated). The individual treatment effect is the difference between these two potential outcomes, Yi(1) − Yi(0). By this we mean that each person is imagined as carrying two possible futures, one for each exposure, before we know which exposure they will actually receive. The word "potential" signals that both outcomes are possible in advance, even though only one will happen. For a disease outcome coded 1 for ill and 0 for well, a person who would fall ill if exposed but stay well if unexposed has Yi(1) = 1 and Yi(0) = 0, so the exposure caused their illness. A person who would fall ill either way has an individual effect of 0, because the exposure made no difference to them.
A thought experiment makes the idea concrete. Imagine you want to know if a vaccine protects against a disease, and you observe a vaccinated person who develops the disease. If you could rewind time and observe the same person in the same period without vaccination, and they did not develop the disease, you would conclude the vaccine actually caused the disease in that individual. Conversely, if they still got the disease without the vaccine, the vaccine was not the cause. The comparison that defines a causal effect is always between the same person, over the same period, under the two exposures.
For a group of exposed people, the counterfactual question takes a standard form: among the people who were exposed, how many would have developed the outcome over the same period if they had not been exposed? For example, in a cohort of households that drank water from a contaminated well, the question is how many of those household members would have become ill over the same month had they not drunk the well water. The question is always about the exposed people themselves, not about the unexposed group, and it cannot be answered directly for any one person, because each person either drank the water or did not.
That last point, that only one of the two potential outcomes is ever observed, is the subject of the next subsection.
6.2 Why Individual Causal Effects Cannot Be Observed
The counterfactual individual in the thought experiment does not exist: you can never observe the same person under two different exposure levels simultaneously. Because each person is either exposed or unexposed, never both, we can only ever observe one of their two potential outcomes, and the other one is missing. Holland (1986) called this the fundamental problem of causal inference: individual causal effects are unobservable. No clever measurement, no improved technology, and no more careful study design can fully solve this problem at the level of a single person (Hernán, 2004). Figure 1.2 lays the problem out for two people: each contributes exactly one observed outcome, and the cell for the exposure they did not receive is a counterfactual.
Exam questions often propose ways around the problem that look convincing at first sight, so the next point is worth fixing firmly.
A Common Trap: Apparent Ways to See an Individual Effect
Comparing a person with a matched partner who was not exposed supplies an observed outcome for a different person, and comparing the person with themselves on a later occasion supplies an outcome for a different period with different conditions, so in both cases the missing outcome is still missing. Even a randomised trial observes each participant under only one exposure; what it gives is a valid comparison between groups.
The counterfactual individual nevertheless remains the ideal that our research methods try to approximate, and the standard response is to give up on the individual treatment effect and estimate something we can learn from data, as the next subsection describes.
6.3 The Average Treatment Effect and Its Stand-In
Rather than asking “what is the effect for this person?” we ask “what is the average effect across a group of similar people?” This quantity is the average treatment effect (ATE) in a population or sample, defined formally in Equation 1.2.
ATE = E[Y(1)] − E[Y(0)]
Equation 1.2. The average treatment effect.
That is, the ATE in Equation 1.2 is the average outcome if everyone were exposed, minus the average outcome if no one were exposed. Equivalently, in epidemiologic notation, it compares p(DE+), the potential frequency of disease if all population members were exposed, with p(DE-), the potential frequency of disease if none were exposed. If these two quantities differ, we infer a causal effect in the population, even though we cannot pinpoint which specific individuals were affected. The reason this works is that averages can be estimated even when individual effects cannot. We never see any single person under both exposures, but we can see the average outcome among people who were exposed and the average outcome among people who were not. For example, if a population would have 10 per cent illness with everyone exposed and 4 per cent with no one exposed, the exposure causes illness in the population as a whole, although we cannot say which of the ill individuals would have stayed well without it.
A real group, like a real person, is observed under only one exposure, so a study uses a comparison group as a stand-in for the missing outcome. In a cohort study the stand-in is the unexposed group: in the well-water example from 6.1, it is the households that did not drink the well water, and their risk is used as the estimate of the risk the exposed group would have had without the exposure. This shift from individual effects to group-level average effects is the conceptual move that powers most modern causal research. Randomized trials, observational studies, policy evaluations, and program evaluations all ultimately rest on the same logic: build two groups (or build a counterfactual comparison) that we can plausibly treat as exchangeable, and compare their average outcomes. The stand-in gives a valid comparison only under that condition of exchangeability, which the next subsection defines.
6.4 Exchangeability and Randomisation
Exchangeability is the condition on which every comparison in this section depends, and it is worth committing to memory in the following form.
Exchangeability
Two groups are exchangeable when the unexposed group's risk equals the risk the exposed group would have had if unexposed, so that the disease frequency in each group would not change if the groups' exposure status were switched.
Put more simply, exchangeable groups are interchangeable: if we swapped the labels, so that the exposed group had been unexposed and the unexposed group had been exposed, we would expect to see the same results. In the well-water example, the households that did not drink the well water are exchangeable with those that did only if they would have fallen ill just as often had they drunk it, which requires them to be alike in age, health, hygiene and every other factor that affects illness. If the unexposed households were, say, younger and healthier, their lower risk would partly reflect those advantages, and the comparison would overstate the harm of the water.
In a perfect experiment, we would randomly assign subjects to exposed and unexposed groups, and randomization creates exchangeability. Because chance alone decides who is exposed, the groups are expected to be alike in every characteristic, measured and unmeasured, that affects the outcome; the assumption is that random assignment balances all known and unknown confounders between groups. Any difference in outcomes can then be attributed to the exposure itself. When groups are exchangeable, comparing p(D|E+) and p(D|E-) gives us the closest possible estimate of the true counterfactual effect, which is why the randomised trial is treated as the gold standard. The estimate is still approximate, however, because in real trials the data come from two different subsets of subjects. Randomisation makes the groups alike on average, but in any one trial chance can leave them somewhat unbalanced, particularly when the trial is small, and the unexposed group remains a different set of people standing in for the missing outcomes of the exposed group.
Randomization is assumed to balance confounders between groups, and the next subsection examines how a confounder distorts the observed association when that balance is absent.
7.1 Confounding and the Limits of Observational Comparisons
A confounder is a variable that is associated with both the exposure and the outcome and can distort the observed association between them (Greenland & Brumback, 2002), making it look stronger or weaker, or creating it entirely. Consider a study of vaccination (E) and disease (D) where a third variable, say a pre-existing health condition (C), independently predicts both who gets vaccinated and who gets the disease. Worked Example 1.4 works through this situation with 20 subjects from the course textbook, comparing the association in the raw data with the association within each level of C.
Worked Example 1.4: Confounding in Action
In the course textbook (Dohoo, Martin, & Stryhn, 2012, table 1.3), 20 subjects are studied. Looking at the raw data, p(D|E+) = 7/13 = 0.54 and p(D|E-) = 3/7 = 0.43, suggesting the exposure might increase disease risk. But when we stratify by the confounder C:
Among C+ subjects: p(D|E+) = 6/9 = 0.67 and p(D|E-) = 2/3 = 0.67
Among C- subjects: p(D|E+) = 1/4 = 0.25 and p(D|E-) = 1/4 = 0.25
Why the crude risks differ. C is unevenly spread across the exposure groups: 9 of the 13 exposed subjects are C+, compared with 3 of the 7 unexposed subjects. C also raises the risk of disease, since 8 of the 12 C+ subjects (0.67) became ill, compared with 2 of the 8 C- subjects (0.25). The exposed group therefore contains a larger share of high-risk C+ subjects, which pulls its crude risk up. In the crude comparison the exposure carries the effect of C, even though it has no effect of its own.
Within each stratum, the exposure has no effect on disease. The apparent association was entirely due to confounding by C, which is why confounders must be controlled in epidemiologic analysis.
Worked Example 1.4 shows that an apparent association can arise entirely from confounding. The same check works in reverse: if an association persists, unchanged, within every level of a third variable, that variable is not responsible for it, and a variable linked only to the outcome cannot be a confounder.
Confounding is the main reason exchangeability is harder to assume in observational studies. In a randomised trial, chance alone decides who is exposed, so exposed and unexposed groups are expected to be alike in every measured and unmeasured characteristic. In an observational study, people choose their exposures, or have them chosen by their circumstances, and the factors that lead to exposure (age, income, health, habits, other exposures) often also affect the outcome. The unexposed group may therefore have a different risk from the one the exposed group would have had, and nothing in the design guarantees otherwise. Because observational studies cannot randomise, they need other ways to deal with this problem, which the next subsection describes.
7.2 Controlling Confounding Without Randomisation
Epidemiologists use several strategies to address confounding in observational studies, and all of them aim to simulate the exchangeability that randomization would provide. Restriction limits the study to one level of the confounder, for example enrolling only non-smokers when smoking is the confounder. Matching makes the exposed and unexposed groups alike on the confounder, for example by pairing each exposed person with an unexposed person of the same smoking status. Stratification examines the association separately within each level of the confounder, as Worked Example 1.4 did for C. Multivariable statistical models adjust for several confounders at once. Restriction and matching act when the comparison groups are formed, whereas stratification and multivariable adjustment act when the data are analysed.
All four strategies act only on the confounders that were thought of, measured and included, whereas randomisation also balances the unmeasured ones. Even a carefully matched and adjusted observational study is therefore not automatically as exchangeable as a trial, and some doubt about unmeasured confounding remains. The same aim of building a credible counterfactual comparison without randomisation also drives the more advanced analytic tools introduced in the next subsection.
7.3 One Counterfactual Logic Behind the Modern Toolkit
Once you accept that causal inference is fundamentally about constructing a credible counterfactual comparison, an estimate of what would have happened in the absence of exposure, many methods used across modern epidemiology, biostatistics, health economics, and policy evaluation start to look like variations on a single theme. Each is a different strategy for approximating the missing potential outcome, although some epidemiologists caution against treating this framework as the only route to causal inference (Vandenbroucke, Broadbent, & Pearce, 2016). Four widely used tools illustrate the point, and each will be explored in much greater depth later in this series. Expand each of the four panels below and, for each tool, identify which group or estimate stands in for the missing counterfactual.
A propensity score is the estimated probability of being exposed given a set of measured characteristics. By this we mean a single number, between 0 and 1, that summarises how likely someone with a particular combination of age, sex, health and other measured traits was to end up exposed. Propensity score matching pairs each exposed person with one or more unexposed people who had a similar probability of being exposed. For example, a smoker whose characteristics gave them a 0.7 chance of smoking would be matched with a non-smoker whose characteristics also gave them about a 0.7 chance, so the two differ in exposure but not in the measured factors that led to it. Matching on one score is far easier than matching on many characteristics at once, which is the practical appeal of the method. The matched unexposed group then serves as the counterfactual stand-in for the exposed group, mimicking what randomization would have done by balancing observed confounders. It is one of the most direct attempts to manufacture exchangeability from observational data.
Regression models, including linear, logistic, Poisson, and Cox, estimate the average difference in outcome associated with exposure while statistically holding other variables constant. Conceptually, regression asks: among people who look the same on measured confounders, what is the average outcome difference between the exposed and the unexposed? When the model is correctly specified and confounders are adequately measured, the regression coefficient on the exposure can be interpreted as an estimate of the average treatment effect. Regression is the workhorse of a later course and underlies many of the more advanced techniques.
Difference-in-differences is a quasi-experimental design used when an exposure (often a policy or program) is rolled out to one group but not another. Rather than comparing exposed and unexposed groups directly, it compares the change over time in the exposed group to the change over time in the unexposed group. The unexposed group's change serves as the counterfactual for what would have happened in the exposed group absent the intervention. This subtracts out stable group differences and shared time trends, isolating the effect of the exposure under the assumption of parallel trends. For example, if a city introduces a tax on sugary drinks and a neighbouring city does not, comparing the two cities' rates of tooth decay directly would be misleading if one city always had more decay than the other. Comparing each city with its own earlier rate removes that fixed difference, and comparing the two changes removes any trend, such as a general rise in decay, that affected both cities alike. The parallel trends assumption states that, without the intervention, the exposed group's outcome would have changed by the same amount as the unexposed group's. If the cities were already heading in different directions before the tax, the method would wrongly attribute that divergence to the policy.
Mediation analysis decomposes the total effect of an exposure on an outcome into a direct effect and one or more indirect effects operating through intermediate variables (mediators). In counterfactual terms, it asks: what would the outcome be if exposure were changed but the mediator were held at its unexposed value, versus if both were changed? Holding the mediator at its unexposed value switches off the indirect route, so whatever effect remains is the direct effect. In the night-shift example from Section 2, this means imagining night workers whose fatigue stayed at the level it would have been on day shifts: any extra injury risk they still carried would be the direct effect of night work, and the rest of the total effect would be the part that travels through fatigue. This allows researchers to estimate both whether an exposure matters and through what pathways it acts, an essential step for designing targeted interventions.
Each of these tools, whether propensity score matching, regression, difference-in-differences, or mediation, is a different answer to the same question: How do we build a credible counterfactual when we cannot randomize? In propensity score matching the matched unexposed group plays that part, in regression it is unexposed people who look the same on measured confounders, in difference-in-differences it is the unexposed group's change over time, and in mediation analysis it is the outcome with the mediator held at its unexposed value, the counterfactual version of the decomposition introduced with the Baron and Kenny approach in Section 2. The methods look very different on the surface, but the underlying logic, comparing observed outcomes to a thoughtfully constructed estimate of what would have happened otherwise, remains the same, and each rests on assumptions that randomisation would not need, such as that all important confounders were measured or that two groups' trends would have run in parallel. Keep this lens in mind throughout the rest of the course.
This section has moved from potential outcomes and the average treatment effect, through exchangeability and confounding, to the analytic tools that approximate the missing counterfactual. The key takeaways below summarise these points, and the knowledge check that follows applies them to new studies.
Key Takeaways
- 6.1 The potential-outcomes, or counterfactual, model defines a causal effect by comparing what actually happened with what would have happened to the same people under a different exposure. For each person i it imagines two potential outcomes, Yi(1) if exposed and Yi(0) if unexposed, and the individual causal effect is the difference Yi(1) − Yi(0). For an exposed group, the counterfactual question takes a standard form: among the people who were exposed, how many would have developed the outcome over the same period if they had not been exposed? When you write it for a question, take the exposed group, the outcome and the time period from the scenario (for example, "how many of the household members who drank the well water would have become ill over the same month had they not drunk it?"), and make sure the question is about the exposed people themselves, not about the unexposed group.
- 6.2 The fundamental problem of causal inference, as Holland called it, is that individual causal effects can never be observed directly. Each person is either exposed or unexposed over a given period, never both, so we see only one of their two potential outcomes and the other is always missing (Figure 1.2). No improvement in measurement or study design can fix this for a single person. Watch for proposals that claim to reveal an individual effect, such as comparing someone with a matched person who was not exposed, or with themselves on a later occasion: a matched partner is a different person and a later occasion has different conditions, so the missing outcome is still missing. Even a randomised trial observes each participant under only one exposure; what it gives you is a valid comparison between groups.
- 6.3 Because individual effects are out of reach, we estimate an average effect for a group instead. The average treatment effect, ATE = E[Y(1)] − E[Y(0)], is the average outcome if everyone were exposed minus the average outcome if no one were exposed, written in epidemiologic notation as the difference between p(DE+) and p(DE-). In practice a comparison group stands in for the missing outcome: in a cohort study, the unexposed group's risk is used as the estimate of the risk the exposed group would have had without the exposure. When asked to name the stand-in, identify the unexposed group in the scenario (for example, the households that did not drink the well water), give its size and risk if the question provides them, and add that the comparison is valid only if the groups are exchangeable.
- 6.4 Exchangeability is the condition that makes the stand-in valid: the unexposed group's risk equals the risk the exposed group would have had without the exposure, so the risk in each group would not change if the two groups' exposures were swapped. Randomisation creates exchangeability because chance alone decides who is exposed, so the groups are expected to be alike in every characteristic, measured and unmeasured, that affects the outcome. That is why the randomised trial is treated as the gold standard and why a difference in outcomes between randomised groups can be attributed to the exposure itself, although the estimate is still approximate because the two groups are different people. When you define exchangeability in an answer, state it in terms of the specific groups in the question (for example, "the non-drinkers' risk equals the risk the drinkers would have had if they had not drunk the water") rather than saying only that the groups are similar.
- 7.1 A confounder is a variable that is associated with both the exposure and the outcome and can distort the crude association between them, making it look stronger or weaker, or creating it entirely. Worked Example 1.4 shows the extreme case: the crude risks (0.54 among the exposed and 0.43 among the unexposed) suggest an effect, but within each level of C the risks are identical, so the whole apparent association came from C. The same stratified check works in reverse: if the risk ratio stays the same within every level of a third variable, that variable is not responsible for the association, and a variable linked only to the outcome cannot be a confounder. Exchangeability is harder to assume in observational studies because people choose their exposures, or have them chosen by their circumstances, for reasons such as age, income, health and habits that also affect the outcome, and nothing in the design balances those reasons. In an answer, compare the crude measure with the stratum-specific measures, say whether the association disappears, changes or persists, and name the reasons the exposed and unexposed groups in that particular study might differ.
- 7.2 Because observational studies cannot randomise, they try to recreate exchangeability in other ways. Restriction limits the study to one level of the confounder, matching makes the exposed and unexposed groups alike on the confounder, stratification examines the association separately within each level of the confounder (as in Worked Example 1.4), and multivariable models adjust for several confounders at once. All four act only on the confounders that were thought of, measured and included, whereas randomisation also balances the unmeasured ones, so even a carefully matched and adjusted study is not automatically as exchangeable as a trial. When a question asks how to deal with a named confounder, choose a method, say how it would be applied to that variable in that study, and acknowledge that unmeasured confounding may remain.
- 7.3 The main analytic tools for causal questions follow the same counterfactual logic: each is a strategy for building a credible estimate of what would have happened without the exposure when randomisation is not possible. Propensity score matching pairs exposed and unexposed people with a similar estimated probability of exposure, so the matched unexposed group becomes the stand-in; regression compares exposed and unexposed people who look the same on measured confounders; difference-in-differences uses the unexposed group's change over time as the counterfactual trend for the exposed group, assuming parallel trends; and mediation analysis asks what the outcome would be if the exposure changed but the mediator were held at its unexposed value. You do not need to run these methods yet. What you should be able to do is recognise, for any of them, which group or estimate plays the part of the missing counterfactual, and remember that each rests on assumptions that randomisation would not need, such as that all important confounders were measured or that the two groups' trends would have run in parallel.
1. A cohort study follows 600 factory workers for 12 months: 200 work in the paint shop, where they are exposed to a solvent, and 400 work elsewhere in the factory. The question is whether solvent exposure causes frequent headaches. Which is the counterfactual question for the paint-shop workers?
2. In the same factory, a nurse wants to know whether the solvent caused the headaches of one paint-shop worker, Mr. Li. She suggests moving him to an office job next year and seeing whether his headaches stop. Why can this not give Mr. Li's individual causal effect of the solvent?
3. In the same cohort, 50 of the 200 paint-shop workers (25 per cent) and 40 of the 400 other workers (10 per cent) developed frequent headaches over the 12 months. Assuming the two groups are exchangeable, which group stands in for the counterfactual, and what is the estimated average treatment effect of the solvent (the risk among the exposed minus the risk among the unexposed)?
4. Study A randomly assigns 500 older adults to take a vitamin D supplement or a placebo. Study B follows 500 older adults who decided for themselves whether to take vitamin D. Both compare the risk of a fall over one year. Which statement is correct?
5. A cohort study of 500 adults asks whether drinking coffee every day increases the risk of developing a chronic cough over five years. The table divides the adults by smoking status and coffee drinking and gives the number in each group who developed a cough. What do these data show about the crude risk ratio for coffee?
| Smoker | Daily coffee | Total | Cough |
|---|---|---|---|
| Yes | Yes | 200 | 20 |
| Yes | No | 50 | 5 |
| No | Yes | 50 | 1 |
| No | No | 200 | 4 |
6. Four research teams study daily coffee drinking and chronic cough, and each handles confounding by smoking in a different way. Team 1 enrols only non-smokers. Team 2 pairs each coffee drinker with a non-drinker of the same smoking status. Team 3 calculates the risk ratio separately for smokers and for non-smokers. Team 4 fits a regression model that includes smoking alongside coffee drinking. Which list names the four strategies in order?
7. City X banned smoking on restaurant patios in 2022; nearby City Y, which is similar, did not. Researchers compare the change in asthma emergency visits from 2021 to 2023 in City X with the change over the same years in City Y. Which analytic tool is this, and what serves as the counterfactual?
8. A city health unit follows 600 adults aged 70 and over for six months: 200 who chose to attend free balance classes and 400 who did not. Overall, 5.0 per cent of attenders and 10.0 per cent of non-attenders had a fall needing medical care. Among adults who used a walking aid, 12.0 per cent of attenders and 15.0 per cent of non-attenders fell; among adults with no walking aid, 4.0 and 5.0 per cent fell. Walking-aid use was recorded before the classes began, and far more non-attenders (50 per cent) than attenders (12.5 per cent) used one. Which statement is correct?
9. In the same study of balance classes, a colleague says: 'We followed attenders and non-attenders in the same way for the same six months, so the non-attenders are as good a comparison group as the control group of a randomised trial.' Which response is best?
✦ Pass the knowledge check with 100% to continue
Lesson Review & Final Assessment
⏱ Estimated time: 15 minutes
Bringing It All Together
This lesson laid the conceptual foundation for designing and analysing epidemiologic studies. You moved from a working definition of epidemiology and a brief history of causal thinking into the formal logic of scientific inference, then into the language epidemiologists use to talk about causes, such as component causes, sufficient causes, and causal webs, and finally into the counterfactual framework that underwrites modern causal inference.
The threads pulled together here are deliberately abstract because the rest of the course is not. Sampling, questionnaire design, measures of disease frequency, screening, measures of association, and study design choices all assume you already know why a research question is causal and what a confounder is. As you work through the final assessment, treat the takeaways below as the vocabulary the next seven lessons will keep using.
Key Takeaways from this lesson
- You can now describe epidemiology as the study of the distribution and determinants of health in populations, whose central goal is to identify causes, especially modifiable ones, that prevention can act on. You can also trace how causal thinking moved from miasma and germ theory, through John Snow's demonstration that cholera could be prevented about 30 years before its agent was isolated, to the multifactorial models used for chronic disease today. The practical reminder: in the modern view almost every outcome has several causes, so the lack of a single identifiable agent never means that a disease has no identifiable causes.
- You can now tell inductive reasoning (from repeated observations to a general conclusion) from deductive reasoning (from a hypothesis to a test that tries to refute it), and explain how Bayesian thinking updates prior knowledge with new evidence. You can also follow a study from the source population through sampling, the measurement of exposures and outcomes, and the handling of extraneous variables to causal inference. When you read a study description, locate the problem on that path: trouble with who got into the study points to selection bias, and a third variable linked to both the exposure and the outcome points to confounding.
- You can now read a DAG: name the exposure and the outcome, classify every other variable as a confounder (fork), a mediator (chain), a collider or none of these, and choose the adjustment set for a total effect. You can explain why conditioning on a collider, including restricting the sample to one of its levels, creates selection bias, and how a DAG (which says what to adjust for) differs from mediation analysis (which estimates how much of the effect runs through a mediator). The reminder for exam questions: name the structure behind each classification, adjust for confounders only, and leave mediators and colliders alone, both in the analysis and when deciding who enters the sample.
- You can now define necessary, sufficient and component causes and use them to classify the causes of a described disease, remembering that one factor can fit more than one term, as an infectious agent is both necessary and a component of every sufficient cause. You can explain why the same exposure shows different risk ratios in populations with different prevalences of its causal complements, and tell direct from indirect causes in a causal web. The most useful reminder: most exposures are component causes that need complements, so a weak or null association where a complement is missing does not mean the exposure can never cause disease.
- You can now use the Bradford Hill viewpoints as aids to judgement to argue whether an observed association is likely to be causal. Start with temporality, the only strict requirement, then support a clearly stated conclusion with the viewpoints the evidence actually speaks to, saying what the evidence shows for each. Remember that temporality is necessary but not sufficient, and that a convincing argument does not need to tick all nine viewpoints.
- You can now state the counterfactual question for an exposed group (how many of the exposed would have developed the outcome over the same period had they not been exposed), explain why individual causal effects can never be observed, and name the unexposed comparison group that stands in for the missing outcome. You can define exchangeability and explain that randomisation creates it by balancing measured and unmeasured characteristics. In an answer, write the question and the exchangeability condition in terms of the specific groups, outcome and time period in the scenario.
- You can now define a confounder, use a stratified comparison to judge whether a third variable explains an association, and explain why exchangeability is harder to assume when people choose their own exposures. You can describe how restriction, matching, stratification and multivariable adjustment address confounding, and recognise that propensity scores, regression, difference-in-differences and mediation analysis rest on the same counterfactual logic. The key reminder: these methods deal only with what was measured, or rest on assumptions the design does not guarantee, so an observational study is never automatically as exchangeable as a randomised trial.
Final Knowledge Assessment
Complete the following 16-question assessment. A score of 100% is required to complete the lesson. You may retake the assessment as many times as needed.
1. A colleague argues: 'No single microorganism explains type 2 diabetes, so epidemiology cannot identify its causes.' Which response reflects the modern view of causation described in this lesson?
2. Over ten years, a family doctor notices that patients who drink green tea every day seem to catch fewer colds, and she tells her patients that green tea prevents colds. Which statement best describes her reasoning and its limit?
3. A DAG for the question 'Does living near a busy road (A) cause asthma in children (B)?' contains these arrows: C → A and C → B, where C is household income; A → D → B, where D is exposure to traffic pollution; E → B, where E is a family history of asthma; and A → F ← B, where F is enrolment in a lung-health screening programme that invites children who live near busy roads and children referred with asthma. How should C, D, E and F be classified?
4. For the DAG described in Question 3, which set of variables should be adjusted for to estimate the total effect of living near a busy road (A) on asthma (B)?
5. A study asks whether heavy smartphone use at night (X) causes poor school grades (Y) among teenagers. In the team's DAG, both heavy night-time phone use and poor grades lead parents to book an appointment with the school counsellor (Z), and the only arrows at Z are X → Z and Y → Z. A colleague finds that counsellor appointments are associated with both X and Y and says, 'Z is associated with both the exposure and the outcome, so it is a confounder and we must adjust for it.' What is wrong with this reasoning?
6. A team wants the total effect of a community salt-reduction programme (X) on strokes (Y). The programme lowers blood pressure (M), and lower blood pressure reduces strokes. In the analysis, the team adjusts for each person's blood pressure at follow-up. What is the consequence?
7. Oysters from one harvest area contaminated with Vibrio parahaemolyticus were sold to two restaurants. Restaurant P served them raw, and the risk ratio for illness among diners who ate oysters there was 7.0. Restaurant Q served the same oysters only deep-fried, and the risk ratio there was 1.1. Which classification of the bacterium and of eating contaminated oysters is correct?
8. Two well-conducted cohort studies examine the same exposure and the same disease. In Region North the risk ratio is 4.0; in Region South it is 1.6. A colleague says, 'A true cause has the same risk ratio everywhere, so one of these studies must be wrong.' Which response is best?
9. A causal web for West Nile virus illness includes this sequence of links: Standing water in yards and ditches → Mosquito breeding → Bites from infected mosquitoes → Infection with West Nile virus → Illness. A town council is debating a programme to drain standing water. Which statement is correct?
10. A one-time survey of 2,000 adults finds that those with chronic back pain are about twice as likely to be physically inactive as those without it, and surveys in three other countries found the same pattern. A colleague concludes that inactivity causes chronic back pain, because the association is strong and consistent. What is the most important weakness in this argument?
11. A new splash park opened on a Saturday. Over the next five weeks, 40 children who had played there developed Cryptosporidium infection, which usually causes illness about 7 days after exposure (range 2 to 10 days). The first case began 3 days after the opening, new cases kept appearing at a similar rate each week with no single peak, and the last case began 34 days after the opening. The park stayed open with the same water system throughout. Is this pattern consistent with a single exposure on the opening day?
12. A cohort of 300 hikers on a guided trip is followed for two weeks after the trip: 120 drank untreated stream water and 180 drank only treated water. Which pair gives the counterfactual question for the hikers who drank stream water and the group that stands in for its answer?
13. A colleague says, 'In the hiking cohort, we can measure each hiker's individual causal effect of stream water by comparing them with a hiker of the same age and sex who drank only treated water.' What is wrong with this statement?
14. In an outbreak investigation at a summer festival, the team asks whether eating at one food truck caused gastroenteritis and checks whether age group could explain the association. Which conclusion do the data in the table support?
| Age group | Ate at the truck | People | Ill |
|---|---|---|---|
| Children | Yes | 100 | 30 |
| Children | No | 100 | 10 |
| Adults | Yes | 200 | 24 |
| Adults | No | 200 | 8 |
15. An observational study cannot randomise, so the team plans to control confounding by matching exposed and unexposed people on age and sex and then adjusting for income and smoking in a regression model. A team member says, 'After this, our groups will be just as exchangeable as in a randomised trial.' Which response is best?
16. At a wedding dinner, 90 of 150 guests ate roast beef that had been cooled slowly and warmed only briefly; 36 of them developed diarrhea and cramps, as did 3 of the 60 guests who did not eat the beef. Clostridium perfringens, whose incubation period is usually 8 to 12 hours (range about 6 to 24 hours), was found in stool samples and in leftover beef. The first case began 7 hours after the dinner, cases peaked at about 10 hours, and the last case began 20 hours after it. Two other guests had diarrhea that began on the afternoon before the dinner and are not in the counts above. Which argument is correct?
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