HSCI 341 · Lesson 1

Introduction &
Causal Concepts

Fundamental Epidemiological Concepts and Approaches

Learning objectives for this lesson:

  1. 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.
  2. 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.
  3. 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.
  4. 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.
  5. Use the Bradford Hill viewpoints, with temporality as the only strict requirement, to argue whether an observed association is likely to be causal.
  6. 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.
  7. 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.

Reference

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.

Key Concepts & Ideas
Cause An event, condition, or characteristic that precedes a disease event and without which the disease event either would not have occurred at all or would not have occurred until some later time.
Effect The change in an outcome that is attributable to a cause, typically defined as a contrast between potential outcomes under different exposure conditions.
Counterfactual A “what would have happened” outcome: the outcome the same individual would have experienced under a different (unobserved) exposure condition. Forms the conceptual basis for causal inference.
Potential Outcomes Framework Formal causal inference framework (Neyman-Rubin) that defines the causal effect for an individual as the difference between the outcome they would have under treatment and under control. Only one of the two is ever observed, the “fundamental problem of causal inference.”
Average Treatment Effect (ATE) The expected difference in potential outcomes across the population: E[Y(1) − Y(0)]. Identifiable from data when exchangeability, positivity, and consistency hold.
Exchangeability The condition that exposed and unexposed groups would have had the same risk of the outcome had they swapped exposures (i.e., no unmeasured confounding). Achieved by design via randomization or by adjustment in observational studies.
Sufficient Cause A complete causal mechanism: a minimal set of conditions and events that inevitably produces the disease. Rothman’s “causal pies” depict each sufficient cause as a pie made of component causes.
Component Cause Any one of the factors that, together with others, makes up a sufficient cause. Each “slice” in a Rothman pie is a component cause.
Necessary Cause A component that must be present in every sufficient cause for the disease to occur. Example: Mycobacterium tuberculosis is necessary for tuberculosis.
Causal Pie Model Rothman’s schematic showing each sufficient cause as a pie composed of component causes. Disease can have multiple sufficient causes (multiple pies), and removing any single component breaks that pie.
Web of Causation MacMahon and Pugh’s metaphor for the complex network of interconnected factors (biological, behavioural, environmental, and social) that contribute to disease.
Association vs. Causation Association is a statistical relationship between two variables; causation is a relationship in which changing one would change the other. All causal relationships imply association, but not all associations are causal; chance, bias, and confounding can produce non-causal associations.
Confounding Distortion of an exposure-outcome association by a third variable that is associated with the exposure and independently affects the outcome, without being on the causal pathway.
Directed Acyclic Graph (DAG) A graphical tool that encodes assumed causal relationships among variables using directed arrows, with no directed cycles. Used to identify confounders, mediators, and colliders for proper adjustment.
Collider A variable on which two or more arrows in a DAG converge. Adjusting for a collider opens a non-causal path and can introduce selection bias (collider-stratification bias).
Mediator A variable that lies on the causal pathway between exposure and outcome. Adjusting for a mediator removes part of the causal effect being estimated.
Induction vs. Deduction Induction reasons from specific observations to general principles; deduction reasons from general principles to specific predictions. Modern epidemiology blends both: hypotheses are deduced from theory and tested against inductively gathered data.
Bradford Hill Considerations Nine viewpoints (strength, consistency, specificity, temporality, biological gradient, plausibility, coherence, experiment, analogy) Hill proposed for judging whether an observed association is likely causal. Not a checklist; only temporality is a strict requirement.
Methods & Approaches
Propensity Score Matching A method that matches exposed and unexposed units on their estimated probability of being exposed (given covariates) to mimic the balance achieved by randomization.
Difference-in-Differences A quasi-experimental method that compares the change in outcome over time in a treated group to the change in an untreated control group, removing time-invariant confounding.
Mediation Analysis A statistical approach that decomposes a total effect into direct and indirect (mediated) components. Classical Baron & Kenny approach has been refined by counterfactual-based methods.
Key People
Sir Austin Bradford Hill (1897–1991) British epidemiologist and statistician who articulated the nine considerations for causal inference (1965) and co-led the British Doctors Study linking smoking to lung cancer.
Kenneth Rothman American epidemiologist who introduced the sufficient-component-cause (“causal pie”) model and authored foundational texts on modern epidemiology.
Judea Pearl Computer scientist whose work formalized causal inference using directed acyclic graphs and the do-calculus, bridging statistics, AI, and epidemiology.
Miguel Hernán Epidemiologist at Harvard whose work (with Robins) developed and popularized the potential-outcomes framework, target trial emulation, and modern causal-inference methods.
Sander Greenland Epidemiologist and biostatistician whose work clarified confounding, effect modification, and the use of DAGs in observational research.
Mervyn Susser (1921–2014) South African-American epidemiologist who advanced concepts of causal thinking in epidemiology and championed eco-epidemiology and social determinants frameworks.
Donald Rubin Statistician who developed the formal potential-outcomes (Rubin Causal Model) framework and propensity score methods.
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Section 1

What Is Epidemiology?

⏱ Estimated reading time: 10 minutes

Lesson 1 · HSCI 341

From Reading Evidence to Producing It

An earlier course trained you to evaluate studies. This course teaches you to design them.

Section 1 of 4

What Is Epidemiology?

Definition, purpose, and the long history of causal thinking about disease.

The discipline

Defining epidemiology

Epidemiology studies the distribution and determinants of health and disease in populations, and applies that knowledge to the control of health problems.

What it tracks

Infectious agents, toxins, nutrients, lifestyle factors, social conditions, any exposure that might affect a population's health.

What makes it distinct

The unit of analysis is the population, not the individual patient. Evidence comes from field studies under real-world conditions.

Historical arc

From Hippocrates to miasma

Hippocratic tradition (c. 400 BCE)

Disease attributed to environmental conditions: air, water, and place. A population-level view, even if the mechanism was wrong.

Miasma theory

Foul air from decay causes disease. Wrong about the cause; the sanitary reforms it prompted still reduced infection dramatically.

The germ theory era

Koch, Pasteur, and John Snow

Germ theory established that specific organisms cause specific diseases, reorganizing medicine around identifying the agent for each condition.

Snow's 1854 cholera map predated that knowledge and traced the pattern of deaths to a single water source. His stronger evidence that cholera spreads through water came from comparing death rates in households supplied by two different water companies.

John Snow's 1854 dot map of cholera deaths clustered around the Broad Street pump, London.
Snow's 1854 cholera map. Public domain, via Wikimedia Commons.
Modern causal thinking

From single agents to webs of causation

Chronic disease epidemiology required moving beyond germ theory's one-agent, one-disease logic to models that handle multiple contributing factors.

Bradford Hill (1965) viewpoints

Strength, consistency, specificity, temporality, biological gradient, plausibility, coherence, experiment, analogy. A structured judgment tool, not a mechanical checklist.

Carry forward

What to take into the next section

  • Epidemiology targets modifiable causes because those are the ones prevention and policy can change.
  • Causal thinking expanded from single agents to webs of interacting biological, social, and behavioural factors.
  • That expansion demands rigorous logical tools for moving from observation to causal claims.

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.

Hippocrates
(~400 BC)
Click to learn more
Miasma Theory
(1750–1885)
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John Snow
(mid-1800s)
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Germ Theory
(late 1800s)
Click to learn more
Goldberger & Pellagra
(early 1900s)
Click to learn more
Framingham & Beyond
(mid-1900s)
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Agent-Host-Environment
(1970s)
Click to learn more
One Health
(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.
Knowledge Check: this section

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?

Choosing an inhaler is a treatment decision for one patient, which is the clinician's task. Epidemiology asks about patterns of exposure and outcome across a population, not how to manage an individual case.
This mentions the exposure, but it is still a fact about one child. The epidemiologist's question compares exposure and asthma across many children to look for an association.
The unit of interest is the population: whether highway exposure is associated with asthma across the region's children, and whether that link is causal, is a question about distribution and determinants that policy could act on.
Diagnosing one child's breathing problem is clinical work focused on an individual. Epidemiology studies how health outcomes are distributed across a population and what determines them.
Correct answer: whether living near a highway is associated with more asthma among the region's children, and whether that association is likely to be causal. The information needed is the unit each person is asking about: the doctor's questions concern one patient, while the epidemiologist is looking at a pattern of exposure and outcome across a population. Epidemiology studies the distribution and determinants of health in populations, and its central goal is to identify causal associations between exposures and outcomes, particularly modifiable ones, such as traffic exposure, that policy can act on. Asking whether this particular child lives near the highway is tempting because it mentions the exposure, but it is still a fact about one person, not a comparison across a population. (Section 1, 1.1 What Epidemiology Studies and Why; Objective 1.1)

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?

This puts miasma first, but the Hippocratic tradition of air, water and place dates from about 400 BCE, roughly two thousand years before miasma theory dominated (about 1750 to 1885).
This places germ theory before miasma, reversing their order. Miasma theory dominated from about 1750 to 1885, and germ theory (Pasteur and Koch) replaced it in the late nineteenth century.
Germ theory came late, in the late nineteenth century, not first. The sequence ran from the Hippocratic tradition, through miasma, to germ theory and then to multifactorial webs of causation.
The Hippocratic focus on air, water and place came first, then miasma, then germ theory, and in the twentieth century chronic disease pushed the field towards multifactorial webs of causation.
Correct answer: (i), (ii), (iii), (iv). The information needed is the era each idea belongs to. The Hippocratic tradition (about 400 BCE) blamed air, water and place; miasma theory, dominant from about 1750 to 1885, blamed foul air from decay; germ theory in the late nineteenth century (Pasteur and Koch) tied specific organisms to specific diseases; and in the twentieth century chronic disease pushed the field towards multifactorial models and webs of causation. Putting miasma first is the tempting error, because both it and the Hippocratic view blame the environment, but the Hippocratic tradition is roughly two thousand years older. (Section 1, 1.2 How Ideas About the Causes of Disease Changed; Objective 1.2)

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?

Snow linked cholera to contaminated water using population observation, decades before Vibrio cholerae was isolated, showing that prevention can proceed before the causal agent is known.
This remembers only the map. Snow also compared deaths in households supplied by two water companies, a natural experiment that gave strong evidence for action without knowing the organism.
Snow worked while miasma theory still dominated, but he did not attribute cholera to miasma; his evidence led him to conclude that cholera spread through contaminated water, and acting on that source could prevent cases.
The lesson uses cholera itself, an infection, to show that prevention can precede identification of the agent, so the point is not limited to chronic diseases.
Correct answer: it contradicts the argument. The information needed is what Snow had and what he lacked: he had population data on where deaths occurred and which company supplied each household, but no knowledge of the organism. By pairing those observations with a testable hypothesis, he identified contaminated water as the route of spread, showing that disease can be prevented before its causal agent is known (Goldberger later did the same for pellagra before niacin was identified). The option that his evidence was too weak to act on is tempting if you remember only the map, but his comparison of the two water companies was a natural experiment and gave the stronger evidence. (Section 1, slide 'Koch, Pasteur, and John Snow' and 1.3 John Snow and Prevention Before the Agent Is Known; Objective 1.3)

✦ Pass the knowledge check with 100% to continue

Section 2

Scientific Inference & Key Research Components

⏱ Estimated reading time: 12 minutes

Section 2 of 4

Scientific Inference & Key Research Components

Inductive and deductive reasoning, the structure of an epidemiologic study, directed acyclic graphs, and mediation.

Two modes of reasoning

Induction and deduction

Inductive (Bacon, Jenner)

From specific observations to general conclusions. Useful for discovery, but as Hume noted, repeated association does not prove causation.

Deductive (Popper)

From general hypothesis to specific test. Science progresses by attempting to disprove the null, not by accumulating confirmations.

Bayesian thinking

Prior knowledge and the weight of new evidence

Bayesian analysis formalizes how prior knowledge is updated by new observations. No single study is read in isolation.

All inference is based on the validity of our premises and no inference can be known with certainty.Paraphrase after Thomas Bayes (1764)
Study structure

From source population to causal inference

Source Population Study Group Exposures & Outcomes Causal Inference Confounding, bias, sampling, threaten every arrow
DAGs

Directed acyclic graphs: formalizing your assumptions

A DAG encodes what causes what before you touch the data. Arrows represent direct causal effects; their absence asserts none.

  • Chain: X → M → Y (mediation)
  • Fork: X ← C → Y (confounding)
  • Collider: X → K ← Y (conditioning opens a spurious path)
X C M Y direct
Mediation

Putting numbers on DAG pathways

Total effect decomposition
\[ \color{#0B7B6B}{\text{Total Effect}} = \underbrace{\color{#C2410C}{c'}}_\text{Direct} + \underbrace{\color{#6D28D9}{a \times b}}_\text{Indirect} \]
Total Effect effect of X on Yc' direct effect (not through M)a×b indirect effect through mediator M

Baron & Kenny (1986): three regressions, four conditions. Modern counterfactual mediation (Imai, Pearl, VanderWeele) handles binary outcomes and exposure-mediator interaction without requiring linearity.

Carry forward

What to take into the next section

  • Induction + deduction + Bayesian updating together move from observation to evidence.
  • A study's validity depends on how well every step of the research diagram is executed.
  • A DAG makes causal assumptions explicit, criticizable, and queryable before data analysis begins.

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.

Source Population Sampling (selection bias?) Study Group Exposure Variables Outcome associations Extraneous Variables (confounding & information bias) Analysis & Causal Inferences Outcomes: continuous / dichotomous / nominal / count / time-to-event Units: individuals, groups, areas

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.

X M Y
Chain
M is a mediator
Don't adjust for M
click to learn more
C X Y
Fork
C is a confounder
Adjust for C
click to learn more
X Y Z
Collider
Z is a collider
Never condition on Z
click to learn more

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.

  1. Name the exposure (X) and outcome (Y), and put them on the page with the exposure on the left.
  2. 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.
  3. 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.
  4. 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.
  5. 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.

  1. Step 1. Total effect. Regress Y on X. The slope (call it c) must be significant. This is the total X → Y effect.
  2. 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.
  3. 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.
  4. 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.
Knowledge Check: this section

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?

This reverses the labels. The nurse moves from repeated observations to a general claim, which is induction; the team starts from a hypothesis and deduces a prediction to test, which is deduction.
Both use observations, but the team's approach starts from a stated hypothesis and deduces what it should observe, then tries to reject it. That deductive test is exactly how a hypothesis is tested.
Induction runs from specific observations to a general claim that repetition cannot prove, as Hume noted; the team deduces a prediction from a null hypothesis and tries to refute it, following Popper.
The nurse's reasoning is inductive, not Bayesian, and no number of repeated observations proves a causal effect; repeated association is consistent with causation but cannot establish it.
Correct answer: the nurse reasons inductively and the team reasons deductively. The information needed is the direction of reasoning in each case. The nurse moves from specific repeated observations to a general conclusion, as Jenner did with the milkmaids, and as Hume noted, repeated association is consistent with causation but cannot prove it. The team starts from a general hypothesis, deduces a specific prediction and tries to disprove it, which is Popper's refutationism and the logic behind testing a null hypothesis. Reversing the two labels is the most common slip: induction runs from observations to a general claim, and deduction runs from a general claim to a specific test. (Section 2, 2.1 Inductive and Deductive Reasoning; Objective 2.1)

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?

Bayesian thinking conditions inference on prior knowledge: one small study against fifteen large consistent ones should shift belief only a little, may be an anomaly, and calls for replication.
Recency does not outweigh weight of evidence. Bayesian thinking updates prior knowledge rather than replacing it, and one small study cannot overturn fifteen large, consistent studies.
This is too sceptical. Kuhn's point is that anomalies are weighed against consensus, not ignored; a contradictory result should still move belief somewhat and prompt further study.
One small study is not enough to conclude causation, especially against strong prior evidence. Strength of association is an aid to judgement, not proof, and the finding needs replication.
Correct answer: weigh the new result against the earlier evidence and seek replication. The information needed is how much was already known (fifteen large, consistent studies) and how much the new study adds (one small study). Bayesian thinking treats every inference as conditioned on prior knowledge and asks how much a new study should update it, and Kuhn's point is that a single contradictory observation may be anomalous, so a scientific community weighs it against the existing consensus. Disregarding the study entirely is tempting but too sceptical: a contradictory result should still move belief a little and prompt further work, which is the logic of systematic reviews and meta-analysis. (Section 2, 2.2 Prior Knowledge, Bayesian Thinking and Scientific Consensus; Objective 2.2)

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?

The two threats are reversed. Recruiting in fitness centres affects who enters the study group, which is selection bias; chronic illness is linked to both activity and depression, which is confounding.
Fitness-centre recruitment affects the sampling of the study group from the source population (selection bias), while chronic illness is a third variable tied to both exposure and outcome (confounding).
Chronic illness does not decide who enters the study; it is associated with both less activity and more depression, so it distorts the comparison, which is confounding rather than selection bias.
Sample size addresses random error only. Selection bias and confounding are systematic errors, so a larger study group would reproduce them with more precision rather than remove them.
Correct answer: selection bias, then confounding. The information needed is where each problem enters the study diagram (Figure 1.1): source population, sampling of a study group, exposures and outcomes, extraneous variables, and causal inference. Recruiting only through fitness centres affects who enters the study group, so the group may not represent the region's adults, which is selection bias at the sampling step; chronic illness is a third variable associated with both the exposure (less activity) and the outcome (more depression), so it can distort the comparison, which is confounding. Reversing the two is the tempting error, and a larger sample fixes neither problem, because both are systematic rather than random. (Section 2, 2.3 The Components of an Epidemiologic Study and Figure 1.1; Objective 2.3)

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?

Airway inflammation lies on the chain Vaping → Airway inflammation → Asthma attacks, so it is a mediator, not a fork. Pollen season has one arrow into the outcome, so it is not a collider either.
Peer smoking has arrows into both vaping and asthma attacks, a fork, so it is a confounder; airway inflammation sits on the chain between them and is the mediator. This option swaps the two.
The first two labels are right, but pollen season points only into the outcome. A confounder must be a common cause of exposure and outcome, so pollen season opens no back-door path.
Peer smoking forms a fork (confounder), airway inflammation lies on a chain (mediator), and pollen season affects only the outcome, so it lies on no back-door path and is none of these.
Correct answer: peer smoking is a confounder, airway inflammation is a mediator, and pollen season is none of these. The information needed is the direction of every arrow at each variable. Peer smoking has arrows into both vaping and asthma attacks, a fork (Vaping ← Peer smoking → Asthma attacks), so it is a confounder; airway inflammation sits between them on a chain (Vaping → Airway inflammation → Asthma attacks), so it is a mediator; pollen season has an arrow into the outcome only and none into the exposure, so it lies on no back-door path and is none of these. Calling pollen season a confounder is the tempting mistake: a confounder must be a common cause of the exposure and the outcome, not a cause of the outcome alone. (Section 2, 3.1 Reading a Directed Acyclic Graph and Worked Example 1.1; Objective 3.1)

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?

Controlling every linked variable ignores structure. Stress is a mediator and enrolment is a collider; adjusting for them would remove part of the effect and open a non-causal path.
Age and job type are correct, but stress lies on the chain X → Stress → Y. Adjusting for a mediator removes part of the total effect, which is over-adjustment.
Age and job type each form a fork and open a back-door path, so both are adjusted for; the mediator (stress) and the collider (enrolment) are left alone for the total effect.
Wellness-programme enrolment is a collider (X → enrolment ← Y). Adjusting for a collider opens a non-causal path between X and Y and introduces bias rather than removing it.
Correct answer: {Age, Job type}. The information needed is the role of each variable: age and job type each form a fork (X ← Age → Y and X ← Job type → Y) and open a back-door path, so both must be adjusted for; stress lies on a chain (X → Stress → Y) and is a mediator; and two arrowheads meet at wellness-programme enrolment (X → enrolment ← Y), so it is a collider. For the total effect you block every back-door path and leave mediators and colliders alone. Adding stress is the tempting error, because it would remove the part of the effect that runs through stress (over-adjustment), and adding the collider would open a non-causal path. (Section 2, 3.2 Choosing What to Adjust For and Worked Example 1.1, step 3; Objective 3.2)

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?

Restriction controls confounding only when it is on a confounder. A clinic visit is caused by both activity and depression, so it is a collider, and restricting on it creates bias.
Both activity (injuries) and depression (counselling) lead to clinic visits, so the visit is a collider; restricting the sample to visitors conditions on it and opens a non-causal path, creating selection bias.
A variable need not be the exposure or outcome to bias a result. Because both activity and depression cause clinic visits, restricting to visitors distorts the association between them.
A clinic visit is not on a path from activity to depression; arrows point into it from both. It is a collider, not a mediator, so restricting on it creates bias rather than isolating a direct effect.
Correct answer: it conditions on a collider and creates selection bias. The information needed is the arrows into a clinic visit: activity leads to visits (sports injuries) and depression leads to visits (counselling), so two arrowheads meet there, Physical activity → Clinic visit ← Depression, and restricting the sample to one level of a collider is the same as conditioning on it. Among visitors, active students may be there for an injury, while inactive students are there mostly because they are depressed, so depression is over-represented among the inactive students in the sample and the protective effect of activity is exaggerated. The first option is tempting because restriction is a real tool, but it removes confounding only when you restrict on a confounder; restricting on a collider creates bias. (Section 2, 3.2 Choosing What to Adjust For and Worked Example 1.1, step 4; Objective 3.2)

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?

A DAG is qualitative: it shows that attention lies on the pathway and what to adjust for, but it cannot say how large each path is. Mediation analysis supplies those sizes.
c′ is the direct effect, the part not passing through attention. The indirect effect is c − c′ = 10 − 6 = 4, and because c′ is not near zero the mediation is partial.
Attention is a mediator. Adjusting for it removes the indirect path and estimates the direct effect (c′), not the total effect (c).
The indirect effect is c − c′ = 4 points, 40 per cent of the total; c′ is well above zero, so mediation is partial, and only the quantitative analysis, not the DAG, gives these sizes.
Correct answer: the indirect effect is 4 points and the mediation is partial. The information needed is c, the total effect, and c′, the direct effect that remains when M is added to the regression: the indirect effect is c − c′ = 10 − 6 = 4 points, which is 4 ÷ 10 = 40 per cent of the total, and because c′ is not close to zero the mediation is partial rather than complete. A DAG is a qualitative tool that says attention lies on the pathway and what to adjust for, whereas mediation analysis is the quantitative step that puts a size on each path. Reading c′ = 6 as the indirect effect is the tempting slip: c′ is the direct effect, the part that does not pass through M. (Section 2, 3.3 DAGs and Mediation Analysis; Objective 3.3)

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Section 3

Seeking Causes & Models of Causation

⏱ Estimated reading time: 15 minutes

Section 3 of 4

Seeking Causes & Models of Causation

Component-cause and causal-web models, the Bradford Hill viewpoints, and the population attributable fraction.

What is a cause?

Any factor that changes disease frequency or severity

Causes operate at different levels: biological (organism, gene, toxin), behavioural, and social or environmental. Not all need to be manipulable, but modifiable causes are most actionable for prevention.

Bradford Hill viewpoints (1965)

Strength · Consistency · Specificity · Temporality (the only hard rule) · Gradient · Plausibility · Coherence · Experiment · Analogy

Component-cause model

Rothman (1976): necessary, sufficient, component

Necessary cause

Must be present for disease to occur. M. tuberculosis for TB. Rare in chronic disease.

Sufficient cause

A complete set of conditions that invariably produce disease. Almost never a single factor alone.

Component cause

One factor within a sufficient cause. May appear in multiple sufficient-cause combinations.

Causal complements

Why strength of association is population-specific

Four risk factors for childhood respiratory disease form different sufficient-cause combinations:

STREPRSVStressorsMP

When RSV prevalence rises from 30% to 70% in the population, the risk ratio for STREP drops from 4.83 to 2.93, even though the causal mechanism is unchanged.

Risk Ratio shifts with co-factor prevalence
\[ \color{#0B7B6B}{\text{RR}_{\text{STREP}}} = f\!\left(\color{#C2410C}{\Pr[\text{RSV}]}\right) \]
RRSTREP risk ratio for the STREP exposurePr[RSV] prevalence of the co-factor RSV

Same biology, different epidemiology.

Causal-web model

Direct and indirect causes in a web

Stressors (indirect) STREP / RSV (direct) MP (direct) CRD (outcome)
Population attributable fraction

Levin's formula (1953)

Population Attributable Fraction
\[ \color{#0B7B6B}{AF_p} = \frac{\color{#C2410C}{p_e}(\color{#6D28D9}{RR} - 1)}{\color{#C2410C}{p_e}(\color{#6D28D9}{RR}-1) + 1} \]
AFp population attributable fractionpe prevalence of the exposureRR risk ratio for the exposure

Where pe is the prevalence of exposure and RR is the risk ratio. The AFp for all risk factors of a disease can sum to more than 100% because each case is attributable to every component cause of the sufficient cause that produced it.

Carry forward

What to take into the next section

  • Most disease has many component causes; necessary causes are rare.
  • Causal complements explain why the same exposure appears stronger or weaker across populations.
  • The population attributable fraction bridges individual-level risk ratios and population-level burden.
  • Managing this complexity requires the formal counterfactual logic of a later section.

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.

Necessary Cause ▼

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.

Sufficient Cause ▼

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.

Component Cause ▼

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 CausesSufficient Cause ISufficient Cause IISufficient Cause IIISufficient 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.

▸ Interactive 1.1: INTERACTIVE STORY: HILL'S CAUSATION GAME SHOW Open full screen ↗

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.
Knowledge Check: this section

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?

Causes are not limited to agents acting inside the body. Lifestyle, nutrition, weather and policy act on groups, and any factor that changes the frequency or severity of an outcome counts as a cause.
This confuses a cause with a necessary cause. Most causes are neither necessary nor sufficient; a factor that changes how often an outcome occurs is a cause even if not present in every case.
A cause is any factor that changes the frequency or severity of an outcome, and causes can operate at the population level; the tax was followed by a fall in tooth decay that the comparison city did not show.
This confuses a cause with a sufficient cause. Most causes are components that act with others, so the tax need not prevent all tooth decay on its own to count as a cause.
Correct answer: a cause is any factor that changes the frequency or severity of an outcome, and causes can act at the population level. The information needed is the definition of a cause and the levels at which causes operate: some act inside individuals (a microorganism, a toxin), while others, such as lifestyle, nutrition, weather or policy, act on groups. Here the tax was followed by a fall in the frequency of tooth decay that a similar city did not show, so it fits the definition, and because it is modifiable it is exactly the kind of cause prevention can use. The options that require the tax to be present in every prevented case, or to be enough on its own, confuse a cause with a necessary or a sufficient cause; most causes are neither, but are components that act together with others. (Section 3, 4.1 What Counts as a Cause; Objective 4.1)

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?

Day 1 lies within the 1 to 10 day range. It is the peak, not the first case, that should match the usual 2 to 5 day incubation, and here the peak at days 3 to 4 does.
Temporality is met because all cases began after the event, and the first case, peak and last case all fall within the incubation range, with the peak inside the usual 2 to 5 days, which coheres with a single exposure.
The Bradford Hill viewpoints are aids to judgement, not a checklist that must be fully satisfied. Only temporality is strictly required, and the timing here supports a conclusion.
A count of cases is not the strength of an association, which is measured by a risk ratio. Timing must still be checked, because temporality and coherence with the incubation period carry the argument.
Correct answer: the pattern is consistent with a single exposure at the open house. The information needed is the timing of the first case, the peak and the last case, compared with the incubation period. Temporality, the one strict requirement, is met because every case began after the event; for coherence with the natural history, the first case at day 1 matches the shortest incubation, the peak at days 3 to 4 lies within the usual 2 to 5 days, and the last case at day 9 is within the 10-day maximum, so counting back one usual incubation period from the peak points to the open house. Rejecting the open house because of the early first case is the tempting error: day 1 lies within the range of 1 to 10 days, and it is the peak, not the first case, that should match the usual incubation period (a count of cases is also not the strength of an association, which is measured by a risk ratio). (Section 3, 5.1 Judging Causation with the Bradford Hill Viewpoints and Worked Example 1.3; Objective 5.1)

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?

Listeriosis cannot occur without the bacterium, so it is necessary and part of every sufficient cause; the cheese is neither necessary (other foods) nor sufficient (many eaters stayed well), so it is a component cause.
The terms are not mutually exclusive. A necessary cause is also a component of every sufficient cause, so the bacterium can be both necessary and a component cause.
A sufficient cause invariably produces disease. Many healthy adults ate the cheese and stayed well, so it completes a sufficient cause only with complements such as a susceptible host.
A necessary cause must be present in every case. Some cases ate other contaminated foods, so the cheese is not necessary even though most cases had eaten it.
Correct answer: the bacterium is necessary and a component of every sufficient cause, and eating the contaminated cheese is a component cause. The information needed is who became ill and who did not: listeriosis cannot occur without Listeria, so the bacterium is necessary and appears in every sufficient cause; some cases ate other foods, so the cheese is not necessary; and many people who ate it stayed well, so it is not sufficient. Eating the cheese completes a sufficient cause only together with its complements, such as a large enough dose and a susceptible host (pregnancy or older age). The sufficient-cause option is tempting, but a sufficient cause invariably produces the disease, and the healthy adults who ate the cheese without becoming ill show that it did not. (Section 3, 4.2 Necessary, Sufficient and Component Causes; Objective 4.2)

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?

TownRisk among the exposedRisk among the unexposed
A11.8 per cent2.0 per cent
B17.2 per cent8.0 per cent
The ratios are computed correctly, but the mechanism is the same in both towns. The lower ratio in Town B reflects a higher unexposed risk from the second sufficient cause, not weaker biology.
A smaller risk ratio does not mean no effect. The chemical still raises risk in Town B (17.2 against 8.0 per cent); the ratio is smaller because the unexposed risk is higher there.
Strength of association is population-specific. The same mechanism gives different risk ratios when the other components or sufficient causes are more common in one population.
RR = 11.8 ÷ 2.0 = 5.9 in Town A and 17.2 ÷ 8.0 = 2.15 in Town B; the second sufficient cause is more common in Town B, raising the unexposed risk and pulling the ratio towards 1.
Correct answer: the risk ratios are 5.9 and 2.15, and the difference comes from the more common components of the second sufficient cause in Town B. The information needed is the risk in the exposed and the unexposed in each town: RR = 11.8 ÷ 2.0 = 5.9 in Town A and 17.2 ÷ 8.0 = 2.15 in Town B. In Town B more people develop the condition through the pathway that does not involve the chemical, so the unexposed risk is four times higher (8.0 against 2.0 per cent), and dividing by a larger unexposed risk shrinks the ratio, just as a more common RSV lowered the risk ratio for STREP in Worked Example 1.2. Concluding that the chemical is more harmful in Town A is the tempting error: the strength of association is population-specific, and the same mechanism can give different risk ratios when the prevalence of co-factors differs. (Section 3, 4.3 Causal Complements and the Strength of Association and Worked Example 1.2; Objective 4.3)

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?

This reverses the definitions. A direct cause has no intervening variable before the disease; income acts through housing, paint and ingestion, so it is an indirect cause despite coming first.
Swallowing paint chips and dust has no intervening variable before lead poisoning, so it is the direct cause; the earlier links act through it and are indirect, and removing either kind can prevent cases.
Indirect causes are not necessarily less important for control. Many large-scale efforts, such as repairing old paint, work on indirect causes and still prevent cases.
A cause need not be the toxin itself. Older housing acts through peeling paint and ingestion, which makes it an indirect cause in the web, and acting on it can prevent cases.
Correct answer: swallowing paint chips and dust is the direct cause, and the earlier links are indirect causes. The information needed is the order of the links: 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. Income, older housing and peeling paint all act through the later links, so they are indirect, yet removing one of them, for example by repairing old paint, could still prevent cases. Calling income the direct cause because it comes first reverses the definitions, and the claim that only direct causes are worth targeting is wrong, because many large-scale control efforts work on indirect causes. (Section 3, 4.4 Causal Webs and the Proportion of Disease Explained; Objective 4.4)

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?

Fractions sum to 100 per cent only if every case had exactly one cause. Under the component-cause model a case is attributable to every component of its sufficient cause, so fractions can overlap.
The excess is not uncaused cases. A case produced by a sufficient cause containing several of these exposures would be prevented by removing any one of them, so it is counted in each fraction.
An AFp is the share of cases that would disappear if one exposure were removed; a case whose sufficient cause includes several exposures is prevented by removing any of them, so it counts in several fractions.
The three fractions refer to the same population's cases. They overlap because a single case can be attributable to several components of one sufficient cause, not because the populations differ.
Correct answer: there is no error. The information needed is what an AFp means: the proportion of cases in the population that would disappear if that one exposure were eliminated. A case produced by a sufficient cause that includes inactivity, a low-fibre diet and obesity would be prevented by removing any one of them, so that case is counted in all three fractions, and the fractions can sum to more than 100 per cent. Expecting the fractions to add to 100 per cent is the tempting error; that would be true only if every case had exactly one cause, which the component-cause model says is rarely so. (Section 3, 4.4 Causal Webs and the Proportion of Disease Explained and the slide 'Levin's formula (1953)'; Objective 4.4)

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Section 4

The Counterfactual Concept

⏱ Estimated reading time: 12 minutes

Section 4 of 4

The Counterfactual Concept

Potential outcomes, the fundamental problem of causal inference, and the analytic toolkit that rests on counterfactual logic.

Potential outcomes

The Neyman-Rubin causal model (Rubin, 1974)

Individual treatment effect
\[ \color{#0B7B6B}{\delta_i} = \color{#C2410C}{Y_i(1)} - \color{#6D28D9}{Y_i(0)} \]
δi causal effect for person iYi(1) outcome if exposedYi(0) outcome if unexposed

Yi(1): outcome if person i is exposed.   Yi(0): outcome if person i is unexposed.

The individual treatment effect δi is the causal ideal. As the next slide explains, it is unobservable.

The fundamental problem

Individual effects are unobservable (Holland, 1986)

Individual level

Only one potential outcome is ever observed. The counterfactual is forever missing for any single person.

Population level: ATE

The average treatment effect substitutes a tractable group-level comparison for the unobservable individual effect.

Average Treatment Effect
\[ \color{#0B7B6B}{ATE} = \color{#C2410C}{E[Y(1)]} - \color{#6D28D9}{E[Y(0)]} = \color{#1D4ED8}{p(D_{E+})} - \color{#BE185D}{p(D_{E-})} \]
ATE average treatment effectE[Y(1)] mean outcome if all exposedE[Y(0)] mean outcome if none exposedp(DE+) disease frequency if all exposedp(DE-) disease frequency if none exposed
Randomization

Exchangeability: the logic behind the gold standard

Randomization creates exchangeability: the condition where disease frequency in each group would not change if exposure statuses were swapped.

Under exchangeability, the observed difference in average outcomes equals the true average treatment effect. Randomization achieves this by balancing all confounders, measured and unmeasured, across groups.

Confounding

The threat to exchangeability in observational studies

A confounder is associated with both exposure and outcome, creating a spurious or distorted association.

Crude: p(D|E+) = 0.54, p(D|E−) = 0.43 → apparent risk increase.

Stratified by C: within every stratum, p(D|E+) = p(D|E−). The association was entirely confounding.

C E D spurious association
The modern toolkit

Four tools, one counterfactual logic

Propensity score matching

Pairs exposed and unexposed on probability of exposure, mimicking randomization on observed covariates.

Regression

Holds confounders constant to isolate the average exposure-outcome difference among comparable groups.

Difference-in-differences

Uses an unexposed group's change over time as the counterfactual trend for the exposed group.

Mediation analysis

Decomposes total effect into direct and indirect paths; asks what would happen if the mediator were held fixed.

Carry forward

The counterfactual thread through this whole course

Causal inference is the practice of comparing what happened to what would have happened under a different exposure.Hernán & Robins (2020)

Every method you will learn in this course is a strategy for making that comparison as credible as available data allow. The knowledge check below asks you to apply this logic yourself.

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.

The fundamental problem of causal inference: for each individual only one potential outcome is observedIf exposedIf unexposedIndividualPerson A (exposed)Y(1) observedwe see thisY(0) missingcounterfactualPerson B (unexposed)Y(1) missingcounterfactualY(0) observedwe see thisEach individual contributes exactly one observed outcome; the other is never seen.Causal inference reconstructs the missing cell at the group level.
Figure 1.2. The fundamental problem of causal inference. For any person, only the outcome under the exposure they actually received is observed; the alternative outcome is a counterfactual that must be estimated by comparison across groups.

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.

Propensity Score Matching ▼

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 (Regression Adjustment) ▼

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 (DiD) ▼

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 ▼

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.
Knowledge Check: this section

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?

This is the observed experience of the unexposed, which a study uses as a stand-in for the answer. It is an outcome for different people, not the counterfactual question about the paint-shop workers.
The counterfactual question keeps the same people and the same 12 months and changes only the exposure: how many paint-shop workers would have developed headaches without the solvent.
This is what actually happened to the exposed workers, their observed outcome under exposure. The counterfactual asks about the outcome those same workers would have had without exposure.
This imagines the unexposed workers exposed, which is the counterfactual question for the unexposed group. The question asked is about the paint-shop workers without the solvent.
Correct answer: among the 200 paint-shop workers, how many would have developed frequent headaches over the same 12 months had they not been exposed. The information needed is who was exposed (the paint-shop workers) and the period (12 months); the counterfactual question keeps the same people and the same period and changes only the exposure. Choosing the observed experience of the 400 other workers is the tempting error: that is what a study uses as the stand-in for the answer, but it is an observed outcome for different people, not the counterfactual question itself. The option about the paint-shop workers' actual headaches describes what happened, and the option that imagines the 400 others in the paint shop is the counterfactual for the unexposed group, not for the exposed. (Section 4, 6.1 Potential Outcomes and the Counterfactual Question; Objective 6.1)

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?

An individual causal effect compares Y(1) and Y(0) for the same person over the same period; Mr. Li was exposed this year, so his Y(0) for this year is missing, and next year differs in other ways.
The problem is not measurement error. Holland's fundamental problem is that only one potential outcome per person per period can be observed, so no scale can reveal the missing one.
It is the same person but not the same period. Next year he will be older and his season and workload will differ, so any change in headaches could have other causes.
Sample size does not solve the fundamental problem. Individual effects are unobservable in any study; larger groups help estimate an average effect, not one person's effect.
Correct answer: only one of his two potential outcomes for the same period can ever be observed. The information needed is the definition of an individual causal effect, δi = Yi(1) − Yi(0), which compares the same person over the same period under both exposures. Mr. Li was exposed, so his Y(1) for this year is observed and his Y(0) for this year is missing by definition; next year he will be older, the season and his workload will differ, and any change in his headaches could have other causes. The option that moving him reveals his individual effect is tempting because it is the same person, but it is not the same period, and Holland's fundamental problem of causal inference is that no measurement or design can recover the missing outcome for one person. (Section 4, 6.1 Potential Outcomes and the Counterfactual Question, the vaccine thought experiment, and 6.2 Why Individual Causal Effects Cannot Be Observed; Objective 6.2)

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)?

The arithmetic is right but the roles are reversed. The unexposed workers stand in for what the paint-shop workers' risk would have been without the solvent, not the other way round.
Subtracting case counts ignores group size: 200 and 400 workers cannot be compared by raw counts. The effect is a difference in risks, 50 ÷ 200 = 0.25 minus 40 ÷ 400 = 0.10.
Under exchangeability, the unexposed risk (40 ÷ 400 = 0.10) estimates the exposed group's risk without the solvent, so the average effect is 0.25 minus 0.10 = 0.15, or 15 extra cases per 100 workers.
The fundamental problem rules out individual effects, not group averages. With an exchangeable comparison group, the average treatment effect can be estimated from the two groups' risks.
Correct answer: the unexposed workers stand in, and the estimated average effect is 0.15. The information needed is the risk in each group: 50 ÷ 200 = 0.25 among the exposed and 40 ÷ 400 = 0.10 among the unexposed. The unexposed group's risk is used as the estimate of the risk the paint-shop workers would have had without the solvent, so the average treatment effect, p(DE+) − p(DE-), is estimated as 0.25 − 0.10 = 0.15, which is valid only under exchangeability. Subtracting case counts (50 − 40) is the tempting error: the groups are different sizes, so they must be compared as risks, and the fundamental problem rules out individual effects, not group averages. (Section 4, 6.3 The Average Treatment Effect and Its Stand-In; Objective 6.3)

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?

Having a comparison group over the same period does not create exchangeability. In Study B, the reasons people chose vitamin D may also affect falls, so the groups may differ.
Exchangeability does not mean participants can switch groups. It means each group's risk would be unchanged if the groups swapped exposures, which randomisation makes plausible.
Balance on a few measured variables such as age and sex cannot rule out differences in unmeasured ones, such as health awareness or exercise, that also affect falls.
Random assignment makes groups alike on average in measured and unmeasured characteristics, creating exchangeability; when people choose their exposure, those same reasons may affect falls.
Correct answer: exchangeability can be assumed in the randomised Study A but is harder to assume in Study B. The information needed is how exposure was decided in each study. Exchangeability means the risk in each group would be unchanged if the groups swapped exposures; random assignment makes the groups alike, on average, in both measured and unmeasured characteristics, which is why the randomised trial is the gold standard. In Study B people chose their exposure, and the same factors that lead someone to take vitamin D (health awareness, exercise, diet, income) may also lower their risk of falling, so the non-users' risk may not be the risk the users would have had. Showing that the groups have the same age and sex is tempting reassurance, but balance on a few measured variables cannot rule out differences in unmeasured ones. (Section 4, 6.4 Exchangeability and Randomisation and 7.1 Confounding and the Limits of Observational Comparisons; Objectives 6.4 and 7.1)

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?

SmokerDaily coffeeTotalCough
YesYes20020
YesNo505
NoYes501
NoNo2004
The stratum results cannot be ignored. Within smokers and within non-smokers the risk ratio is 1.0, so the crude 2.3 reflects smoking rather than an effect of coffee.
Crude risks of 21 ÷ 250 and 9 ÷ 250 give 2.3, but the risk ratio is 1.0 within each smoking group; most coffee drinkers smoke, so the crude association reflects confounding by smoking.
A mediator would require coffee to cause smoking. Smoking is associated with coffee and causes cough, so it is a confounder, and the crude ratio of 2.3 is distorted, not a total effect.
This divides the risk in coffee-drinking smokers by the risk in non-drinking non-smokers, mixing the two strata. Comparisons must be made within the same level of smoking.
Correct answer: the crude risk ratio of 2.3 is due to confounding by smoking. The information needed is the risk in each row and in the totals: coffee drinkers 21 of 250 (0.084) and non-drinkers 9 of 250 (0.036) give a crude RR of 0.084 ÷ 0.036 = 2.3, while within smokers the RR is (20 ÷ 200) ÷ (5 ÷ 50) = 0.10 ÷ 0.10 = 1.0 and within non-smokers (1 ÷ 50) ÷ (4 ÷ 200) = 0.02 ÷ 0.02 = 1.0. Most coffee drinkers smoke (200 of 250) and smoking raises the risk of cough, so in the crude comparison coffee carried the effect of smoking; once smoking is held constant the association disappears, as in Worked Example 1.4. Calling smoking a mediator is the tempting error, because that would require coffee to cause smoking, and the 5.0 option compares coffee-drinking smokers with non-smokers who do not drink coffee, mixing the two strata. (Section 4, 7.1 Confounding and the Limits of Observational Comparisons and Worked Example 1.4; Objective 7.1)

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?

Team 1 limits the study to non-smokers, which is restriction, and Team 2 builds pairs with the same smoking status, which is matching. This option swaps the first two.
Team 2 forms comparison pairs, which is matching, while Team 3 analyses within each level of smoking, which is stratification. Matching acts when groups are formed; stratification acts at analysis.
Enrolling one smoking level is restriction, pairing on smoking is matching, separate analysis by smoking is stratification, and including smoking in a model is multivariable adjustment.
No team assigns coffee drinking by chance, so none uses randomisation. Team 4 includes smoking in a regression model, which is multivariable adjustment, not restriction.
Correct answer: restriction, matching, stratification, multivariable adjustment. The information needed is what each team does with the confounder: limiting the study to one level of smoking is restriction, building pairs that share smoking status is matching, analysing within each level of smoking is stratification, and putting smoking into a statistical model with the exposure is multivariable adjustment. Each strategy tries to recreate, for smoking, the exchangeability that randomisation would have provided, and none of them is randomisation, because no team assigns coffee drinking. Confusing matching with stratification is the most common slip: matching acts when the comparison groups are formed, whereas stratification acts when the data are analysed. (Section 4, 7.2 Controlling Confounding Without Randomisation; Objective 7.2)

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?

Comparing City X's change with the change over the same years in a similar unexposed city is difference-in-differences; City Y's trend stands in for what would have happened in City X without the ban.
Using City X's own earlier level is a simple before-and-after comparison, which would credit the ban with any change that would have happened anyway. City Y's trend supplies the counterfactual.
Propensity score matching pairs individuals with similar probabilities of exposure. Here whole cities are compared on their change over time, which is difference-in-differences.
Mediation analysis splits an effect into direct and indirect paths through a mediator. Here City Y is an unexposed comparison over time, not an indirect pathway of the ban.
Correct answer: difference-in-differences, with City Y's change as the counterfactual trend. The information needed is what is being compared: a change over time in the exposed city against a change over the same period in a similar unexposed city. The unexposed city's change stands in for what would have happened in City X without the ban, which subtracts out stable differences between the cities and trends they share, under the assumption that the two cities would otherwise have followed parallel trends. Using City X's own earlier level as the counterfactual is the tempting error: a simple before-and-after comparison would credit the ban with any change that would have happened anyway, such as a mild allergy season across the region. (Section 4, 7.3 One Counterfactual Logic Behind the Modern Toolkit, difference-in-differences; Objective 7.3)

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?

A benefit in both strata does not make the crude value correct. The stratum ratios are 0.80, not 0.50, so the crude ratio is confounded and overstates the benefit.
This divides the non-attenders' risk by the attenders', inverting the ratio. Risk among the exposed (attenders) over the unexposed is 5.0 ÷ 10.0 = 0.50, a lower risk, not a doubling.
Crude 5.0 ÷ 10.0 = 0.50, but 12.0 ÷ 15.0 and 4.0 ÷ 5.0 both give 0.80; walking-aid use is linked to attendance and to falls, so confounding made the classes look more protective than they were.
Walking-aid use was recorded before the classes began, so the classes cannot have caused it and it cannot be a mediator. It is a confounder, and the crude 0.50 is distorted.
Correct answer: the crude risk ratio is 0.50, it is 0.80 within both walking-aid groups, and the crude ratio is confounded by walking-aid use. The information needed is the risk among attenders divided by the risk among non-attenders, overall and within each group: 5.0 ÷ 10.0 = 0.50 overall, 12.0 ÷ 15.0 = 0.80 among walking-aid users and 4.0 ÷ 5.0 = 0.80 among non-users. Walking-aid use is linked to the exposure (far more non-attenders used one) and to the outcome (users fell more often in both groups), so the non-attenders included more frail adults and the crude comparison made the classes look more protective than they were; as in Worked Example 1.4, comparing the crude result with the results within each level of the third variable reveals the confounding, although here the association shrinks rather than disappearing. Keeping the crude 0.50 because both groups also show a benefit is the tempting error, and walking-aid use cannot be a mediator, because it was recorded before the classes began. (Section 4, 7.1 Confounding and the Limits of Observational Comparisons and Worked Example 1.4; Objective 7.1)

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?

Identical follow-up makes the measurement of falls comparable, not the groups exchangeable. Adults chose to attend for reasons, such as frailty, that also affect their risk of falling.
A larger sample reduces random error, not confounding. Precise estimates from non-exchangeable groups remain biased by the reasons people chose to attend.
This overstates the limit. A cohort study can estimate an average effect if the groups are exchangeable, and methods such as stratification or adjustment address measured confounders.
Equal follow-up protects outcome measurement, but attendance was chosen for reasons that also affect falls; methods for measured confounders such as walking-aid use help, though unmeasured differences may remain.
Correct answer: disagree, because equal follow-up does not make the groups exchangeable. The information needed is how attendance was decided: the adults chose it, and the reasons behind that choice (frailty, walking-aid use, general health, fear of falling, motivation) also affect the risk of a fall, so the non-attenders' risk need not equal the risk the attenders would have had without the classes. In a randomised trial chance alone decides who attends, which balances measured and unmeasured characteristics on average; here the study can only address the confounders it measured, for example by restricting to adults without a walking aid, matching or stratifying on walking-aid use, or adjusting for it with age and earlier falls. Agreeing because both groups were followed identically is the tempting error: identical follow-up protects the measurement of the outcome, not the comparability of the groups, and a larger sample reduces random error, not confounding. (Section 4, 6.4 Exchangeability and Randomisation and 7.2 Controlling Confounding Without Randomisation; Objectives 6.4, 7.1 and 7.2)

✦ Pass the knowledge check with 100% to continue

Section 5

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

  1. 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.
  2. 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.
  3. 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.
  4. 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.
  5. 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.
  6. 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.
  7. 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.

Final Assessment: 16 Questions

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?

One-agent, one-disease logic explained many infections but not chronic disease. The field moved to multifactorial models in which several interacting factors can each be studied as causes.
Multicausality does not mean anything causes anything. The modern view still requires evidence that each factor changes the frequency or severity of the outcome.
Chronic diseases are not determined by genes alone. The modern view combines biological, behavioural, social and environmental causes, and modifiable non-genetic factors are prime targets for prevention.
Almost every outcome has several causes, so the lack of a single agent does not mean a disease has no identifiable causes; each factor in the web of causation can be studied.
Correct answer: the colleague is wrong, because chronic diseases have many interacting causes, each of which can be studied. The information needed is how causal thinking changed after germ theory: one-agent, one-disease logic explained many infections but not heart disease, cancer or diabetes, so the field moved, through studies such as Framingham, to multifactorial models and the web of causation, accepting that almost every outcome has several causes and that one cause can have several effects. Epidemiology then looks for the modifiable causes within that web, because those are the ones prevention can act on. The 'anything can cause anything' option is a tempting misreading of multicausality; the modern view still demands evidence that each factor changes the frequency or severity of the outcome. (Section 1, slide 'From single agents to webs of causation' and 1.2 How Ideas About the Causes of Disease Changed; Objective 1.2)

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?

Moving from many observations to a general claim is induction, and repeated association cannot prove causation, as Hume noted; the claim should be tested by trying to refute a specific prediction.
She starts from observations of her patients, not from a general rule, so her reasoning is inductive. Ten years of observation is still consistent with other explanations and proves nothing.
The label is right but the conclusion fails. No number of repeated associations turns into proof; tea drinkers may differ in other habits, so the claim needs testing.
Bayesian reasoning weighs new evidence against prior knowledge, but it never makes a conclusion certain, and her reasoning from repeated observations is inductive.
Correct answer: inductive reasoning, which cannot by itself prove causation. The information needed is the direction of her reasoning: she moves from many specific observations to a general claim, as Bacon described and as Jenner did with milkmaids and cowpox. As Hume noted, repeated association does not prove causation (the tea drinkers may, for example, differ in other habits), so the claim needs a test: a specific prediction that a study tries to disprove (Popper), with the result weighed against what is already known (Bayes). The option that enough repetitions turn an association into proof is the tempting error; no number of repeated observations gives logical certainty. (Section 2, 2.1 Inductive and Deductive Reasoning; Objective 2.1)

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?

E points only into B, so it is a cause of the outcome alone and opens no back-door path. A confounder must be a common cause of both the exposure and the outcome.
This swaps C and D. C has arrows into both A and B, a fork, so it is a confounder; D lies on the chain A → D → B, so it is a mediator.
C forms a fork (confounder), D lies on the chain from A to B (mediator), E affects only B (none of these), and two arrowheads meet at F (collider).
F has arrows coming in from both A and B (A → F ← B), so it is a collider. A mediator needs a chain with an arrow out of it into the outcome.
Correct answer: C is a confounder, D a mediator, E none of these, and F a collider. The information needed is the direction of the arrows at each variable. C has arrows into both A and B (A ← C → B), a fork; D lies on A → D → B, a chain through which the effect travels; E points only into B, so it is on no back-door path and forms none of the three structures; and two arrowheads meet at F (A → F ← B), which makes it a collider. Labelling family history a confounder is the tempting mistake: it affects the outcome but not the exposure, so it cannot open a back-door path. (Section 2, 3.1 Reading a Directed Acyclic Graph and Worked Example 1.1; Objective 3.1)

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)?

D is a mediator on A → D → B. Adjusting for it removes the part of the effect running through traffic pollution, which is over-adjustment when the total effect is wanted.
Being linked to A or B does not justify adjustment. D is a mediator and F is a collider; including them removes part of the effect and opens a non-causal path.
Adjusting for the collider F does not remove selection bias; it creates it, by opening the non-causal path A → F ← B. Only C needs adjustment.
Only C opens a back-door path, so adjusting for C is enough; E causes only the outcome, so adding it creates no bias, while adjusting for D or F would introduce over-adjustment or collider bias.
Correct answer: {C}. The information needed is which variables open back-door paths: only household income (C) does, through the fork A ← C → B, so it must be adjusted for. Traffic pollution (D) is a mediator, and adjusting for it would remove part of the effect being estimated; screening-programme enrolment (F) is a collider, and adjusting for it would open the non-causal path A → F ← B; family history (E) causes the outcome only, so adding it, {C, E}, introduces no bias but is not needed to remove confounding. Adjusting for everything linked to A or B is the tempting error: the structure of the DAG, not the number of arrows, decides what belongs in the adjustment set. (Section 2, 3.2 Choosing What to Adjust For; Objective 3.2)

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?

Association with both exposure and outcome does not identify a confounder. A collider is associated with both precisely because both cause it; a confounder must be a common cause.
Both X and Y cause appointments, so arrowheads meet at Z, a collider; adjusting for it, or analysing only students who saw the counsellor, opens a non-causal path and creates bias.
A mediator needs the chain X → Z → Y, with an arrow from Z into grades. Here Z has only incoming arrows, so it is a collider, not a mediator.
Sample size is not the issue. Adjusting for a collider introduces bias at any sample size, because it opens a non-causal path between X and Y.
Correct answer: Z is a collider and should be left alone. The information needed is the direction of the arrows, not just the presence of an association: both night-time phone use and poor grades cause appointments, so two arrowheads meet at Z (X → Z ← Y). A collider is associated with both the exposure and the outcome precisely because both cause it, which is why an association alone cannot identify a confounder; a confounder must be a common cause, with arrows out of it into both. Adjusting for Z, or analysing only students who saw the counsellor, opens the non-causal path through Z and creates selection bias, and calling Z a mediator is also wrong, because a mediator needs the chain X → Z → Y and here Z has no arrow into grades. (Section 2, 3.1 Reading a Directed Acyclic Graph, Collider card, and 3.2 Choosing What to Adjust For; Objectives 3.1 and 3.2)

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?

Blood pressure is a mediator on X → M → Y; controlling for it blocks the indirect path and removes part of the effect, so the estimate is closer to the direct effect than the total effect.
M is associated with X and Y, but because the programme causes it, it lies on the causal pathway, not on a back-door path. Adjusting for it removes effect rather than confounding.
A collider has arrows from both exposure and outcome pointing into it. Here the programme causes blood pressure and blood pressure causes strokes, which is a chain, so M is a mediator.
More adjustment is not always better. Adjusting for a mediator removes part of the total effect, and adjusting for a collider opens a non-causal path; the DAG decides what belongs in the set.
Correct answer: it blocks the indirect path, which is over-adjustment. The information needed is the structure X → M → Y, a chain in which blood pressure is a mediator. Controlling for a mediator removes the part of the effect that travels through it, so the result estimates something closer to the direct effect, which is appropriate only when the direct effect is the question; measuring how much of the effect runs through M is the job of a mediation analysis, such as Baron and Kenny's c − c′. Treating M as a confounder is the tempting error: it is associated with both X and Y, but because the programme causes it, it lies on the causal pathway rather than on a back-door path. (Section 2, Chain (Mediator) card and 3.3 DAGs and Mediation Analysis; Objectives 3.2 and 3.3)

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?

A sufficient cause invariably produces disease. Diners who ate the same contaminated oysters deep-fried had a risk ratio near 1, so eating them was not sufficient without complements.
The bacterium is necessary for this illness wherever it occurs. The risk ratio near 1 at Restaurant Q shows that cooking removed a causal complement, not that the bacterium stopped being a cause.
The illness cannot occur without the bacterium, so it is necessary; eating contaminated oysters is a component cause that completes a sufficient cause only with complements such as eating them raw.
This reverses the roles. The bacterium is the necessary cause; eating contaminated oysters is not necessary, because other seafood can carry the bacterium.
Correct answer: the bacterium is necessary and a component of every sufficient cause, and eating contaminated oysters is a component cause. The information needed is the contrast between the two restaurants: the same contaminated oysters gave a strong association where they were eaten raw and almost none where they were cooked. The illness cannot occur without the bacterium, so it is necessary; eating the oysters is not necessary (other seafood can carry the bacterium) and not sufficient, because it completes a sufficient cause only with complements such as bacteria surviving in raw oysters, a large enough dose and a susceptible diner, and at Restaurant Q, where cooking removed a complement, the risk ratio fell to about 1. The sufficient-cause option is the tempting error: a sufficient cause invariably produces the disease, and the cooked oysters show that the contaminated food did not. (Section 3, 4.2 Necessary, Sufficient and Component Causes and 4.3 Causal Complements and the Strength of Association; Objective 4.2)

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?

Strength of association is population-specific, not fixed. The risk ratio depends on how common the causal complements and other sufficient causes are in each population.
An exposure causes disease only with its complements, and the unexposed risk depends on other sufficient causes, so the same mechanism can give risk ratios of 4.0 and 1.6, as with STREP and RSV.
A risk ratio of 1.6 still indicates raised risk, and strength is an aid to judgement, not a threshold. A smaller ratio can reflect more common other sufficient causes.
Differing risk ratios do not require the exposure to be necessary in one region. They arise when complements or other sufficient causes differ in prevalence between populations.
Correct answer: the colleague is wrong, because the strength of association is population-specific. The information needed is what determines a risk ratio in the component-cause model: an exposure produces disease only when its causal complements are also present, and the risk in the unexposed depends on how common the other sufficient causes are, so both risks, and therefore their ratio, depend on how common the other components are in each population. Two valid studies can therefore find 4.0 and 1.6 with no difference in biology, as Worked Example 1.2 showed when the risk ratio for STREP fell from 4.83 to 2.93 as RSV became more common. Treating a risk ratio below 2 as proof of no effect is also wrong; strength is an aid to judgement, not a threshold. (Section 3, 4.2 Necessary, Sufficient and Component Causes with Table 1.1, and 4.3 Causal Complements and the Strength of Association with Worked Example 1.2; Objective 4.3)

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?

Indirect causes can be targeted for control. Draining standing water removes a link that acts through mosquito breeding and bites, so it can prevent illness without being the direct cause.
Coming first does not make a factor the direct cause. A direct cause has no intervening variable; standing water acts through breeding and bites, so it is indirect.
Standing water and breeding act through intervening links, so they are indirect causes; removing an indirect cause can still prevent disease, as many large-scale control efforts do.
The other factors are links in the causal web, not confounders. Each is an indirect cause acting through later links, and acting on them can prevent illness.
Correct answer: standing water is an indirect cause, and acting on it can prevent illness. The information needed is the position of each factor in the web: infection with the virus has no intervening variable before illness, so it is the direct cause, while standing water acts through mosquito breeding and bites, so it is indirect. The causal web shows that disease can be controlled either by preventing the action of a direct cause or by removing an indirect cause, and many large-scale control efforts, like draining breeding sites, work on indirect causes. The option that draining cannot help because standing water is not a direct cause is the tempting error; direct causes are not necessarily more valuable for control. (Section 3, 4.4 Causal Webs and the Proportion of Disease Explained; Objective 4.4)

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?

Specificity is not required, since many real causes, such as smoking, affect several diseases. Failing specificity does not rule out causation.
A one-time survey measures both at the same moment, so it cannot show which came first; temporality is the one viewpoint that must be met, and back pain may have caused the inactivity.
There is no strength threshold below which an association cannot be causal. Strength is an aid to judgement; the more serious problem here is unknown temporal order.
Strength and consistency support a causal argument but do not prove it. Without temporality, which is required, the direction of the association remains unknown.
Correct answer: temporality has not been shown. The information needed is the design: a one-time survey measures inactivity and back pain at the same moment, so it cannot show which came first. Temporality is the one viewpoint that must be satisfied, because a cause cannot follow its effect, and here pain could plausibly cause inactivity; strength and consistency support a causal argument but cannot rescue it while the order is unknown. Failing specificity is the tempting objection, but specificity is not required, since many real causes, such as smoking, affect several diseases. (Section 3, 5.1 Judging Causation with the Bradford Hill Viewpoints; Objective 5.1)

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?

Temporality is necessary but not sufficient. Cases also need timing coherent with the incubation period, and onsets continuing to day 34 cannot come from exposure on the opening day.
The first case alone does not establish a single exposure. A single exposure would end within about 10 days with one peak near day 7; steady cases to day 34 do not fit.
A single exposure would give cases within 2 to 10 days with one peak; steady onsets for weeks past the 10-day maximum fit continuing exposure while the park stayed open.
Day 3 lies within the 2 to 10 day range, so the first case is not too early. The problem is that cases continued long past the maximum incubation, with no single peak.
Correct answer: no, the pattern does not fit a single exposure on the opening day. The information needed is the incubation range (2 to 10 days) and the timing of the first, typical and last cases. A single exposure would produce cases within about 2 to 10 days of the opening, with a steep rise, one peak near day 7 and a fall within about one incubation period; cases continuing at a steady rate until day 34 cannot come from exposure on day 0, but they cohere with children being infected on later visits. The first option is the tempting error: temporality is necessary but not sufficient, so meeting it does not establish a single exposure, and the timing must also cohere with the natural history of the infection. (Section 3, 5.1 Judging Causation with the Bradford Hill Viewpoints and Worked Example 1.3; Objective 5.1)

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?

The counterfactual asks how the same 120 exposed hikers would have fared over the same two weeks without stream water; the 180 unexposed hikers stand in, provided the groups are exchangeable.
This asks about the unexposed group's observed outcome, which is the stand-in, not the counterfactual question for the stream-water drinkers.
Their illness with exposure was observed, but the counterfactual is their outcome without exposure, which can never be observed; a stand-in is therefore needed.
The question is right, but a later trip is a different period with different conditions, so it does not observe the missing outcome for this trip.
Correct answer: the counterfactual question asks how many of the 120 stream-water drinkers would have become ill over the same two weeks without the stream water, and the 180 treated-water drinkers stand in. The information needed is who was exposed (the 120), the period (two weeks) and who was not exposed (the 180). Because the stream-water drinkers' outcome without exposure can never be observed, the unexposed group's risk is used in its place, which is valid only under exchangeability, meaning their risk equals the risk the exposed group would have had without the exposure. Using the same hikers on a later trip is tempting, but a later trip is a different period with different conditions, so it does not observe the missing outcome. (Section 4, 6.1 Potential Outcomes and the Counterfactual Question and 6.3 The Average Treatment Effect and Its Stand-In; Objectives 6.1 and 6.3)

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?

Matching on age and sex compares different people, so it can only support an average comparison, and only if the groups are exchangeable on everything that affects illness.
If the matched hiker also drank stream water, there would be no unexposed comparison at all. The real problem is that each hiker's own unexposed outcome is missing.
Randomised trials create exchangeable groups and estimate average effects, but each participant is still observed under only one exposure, so individual effects remain unobservable.
An individual effect needs the same person's outcomes with and without exposure over the same period; a matched partner is someone else, so matching supports only a group-level comparison.
Correct answer: a matched hiker is a different person, so the individual effect remains unobservable. The information needed is the definition of an individual causal effect: the difference between the same person's outcomes with and without the exposure over the same period, Y(1) − Y(0). A matched partner supplies an observed outcome for someone else, so matching, like any comparison group, can only estimate an average effect, and only if the matched groups are exchangeable on everything that affects illness, not just age and sex. The option that randomised trials reveal individual effects is the tempting error: randomisation creates exchangeable groups and gives a valid average treatment effect, but each participant is still observed under only one exposure. (Section 4, 6.2 Why Individual Causal Effects Cannot Be Observed and 6.3 The Average Treatment Effect and Its Stand-In; Objective 6.2)

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 groupAte at the truckPeopleIll
ChildrenYes10030
ChildrenNo10010
AdultsYes20024
AdultsNo2008
The risk ratio is 3.0 among children (0.30 ÷ 0.10), among adults (0.12 ÷ 0.04) and overall (0.18 ÷ 0.06), so the association persists unchanged and age group does not explain it.
A confounder must be associated with the exposure as well as the outcome. Half of each age group ate at the truck, so age is not linked to the exposure and cannot confound.
An association that persists within each age group points away from confounding by age. Confounding shows when the crude result differs from the results within strata.
0.30 ÷ 0.04 divides children's risk among eaters by adults' risk among non-eaters, mixing strata. The correct crude ratio is 0.18 ÷ 0.06 = 3.0, the same as within each age group.
Correct answer: age group does not explain the association. The information needed is the risk ratio within each age group and overall: (30 ÷ 100) ÷ (10 ÷ 100) = 0.30 ÷ 0.10 = 3.0 among children, (24 ÷ 200) ÷ (8 ÷ 200) = 0.12 ÷ 0.04 = 3.0 among adults, and (54 ÷ 300) ÷ (18 ÷ 300) = 0.18 ÷ 0.06 = 3.0 overall. Because the association persists, unchanged, within every level of age group, age group is not responsible for it; this is the reverse of Worked Example 1.4, where the association vanished within strata. Calling age group a confounder because children had more illness is the tempting error: a confounder must be associated with the exposure as well as the outcome, and here half of each age group ate at the truck (the 7.5 option divides a children's risk by an adults' risk, mixing the strata). (Section 4, 7.1 Confounding and the Limits of Observational Comparisons, Worked Example 1.4 and the paragraph after it; Objective 7.1)

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?

No combination of matching and adjustment guarantees exchangeability. These methods act only on measured, included confounders; an unmeasured factor can still confound.
Sample size reduces random error, not confounding. A precisely estimated model still leaves bias from any confounder that was never measured.
Matching and regression adjustment can be combined. The limitation is that both act only on the confounders that were measured and included.
Matching and adjustment balance only the variables the team measures and includes, whereas randomisation balances measured and unmeasured characteristics by chance.
Correct answer: disagree, because these methods handle only the confounders that were measured and included. The information needed is how each approach builds a counterfactual comparison: randomisation balances measured and unmeasured characteristics by chance, whereas restriction, matching, stratification, multivariable adjustment and propensity scores act only on the variables the team chooses and measures. All of them aim at the same counterfactual comparison as a trial and can make the groups close to exchangeable for those variables, but an unmeasured factor that affects both the exposure and the outcome can still confound the result. A large sample is the tempting reassurance, but more participants reduce random error, not confounding by a factor that was never measured. (Section 4, 7.2 Controlling Confounding Without Randomisation and 7.3 One Counterfactual Logic Behind the Modern Toolkit; Objectives 7.2 and 7.3)

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?

This inverts the ratio, dividing non-eaters' risk by eaters'. Risk among the exposed over the unexposed is (36 ÷ 90) ÷ (3 ÷ 60) = 0.40 ÷ 0.05 = 8.0, a strong positive association.
Risks of 0.40 and 0.05 give a ratio of 8.0; all counted cases began after the dinner and onsets fit the incubation period, and the two earlier cases cannot have come from this meal.
The two earlier cases fell ill before the dinner, so they are not part of this outbreak. They do not violate temporality for the 39 cases that began after it.
This divides all ill guests, including non-eaters, by the non-eaters' risk. Onsets between 7 and 20 hours lie within the 6 to 24 hour range, which fits a single meal.
Correct answer: the risk ratio is 8.0 and the pattern fits a single exposure at the dinner. The information needed is the risk in each group and the timing of the first case, the peak and the last case compared with the incubation period, as in Worked Example 1.3: 36 ÷ 90 = 40.0 per cent of beef eaters and 3 ÷ 60 = 5.0 per cent of non-eaters became ill, a risk ratio of 8.0 (strength); every counted case began after the dinner (temporality); and onsets at 7, 10 and 20 hours lie within the 6 to 24 hour range, with the peak inside the usual 8 to 12 hours (coherence with the natural history). The two guests who fell ill before the dinner cannot have been made ill by a meal they had not yet eaten, so they are not part of this outbreak and do not weaken the conclusion for the other 39. Rejecting the beef because of those two early cases is the tempting error, and the 5.2 option divides all ill guests, including non-eaters, by the non-eaters' risk instead of comparing eaters with non-eaters. (Section 3, 5.1 Judging Causation with the Bradford Hill Viewpoints and Worked Example 1.3; Objective 5.1)

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