HSCI 341 — Lesson 12

Confounding and Causal Inference

Fundamental Epidemiological Concepts and Approaches

Kiffer G. Card, PhD, Faculty of Health Sciences, Simon Fraser University

Learning objectives for this lesson:

  • Apply criteria to identify potential confounders in observational studies
  • Use restricted sampling and matching to prevent confounding
  • Implement matching in both cohort and case-control study designs
  • Use causal diagrams (DAGs) to identify confounders needing control
  • Apply stratified analysis (Mantel-Haenszel) to control confounding and assess interaction
  • Understand propensity scores, instrumental variables, and marginal structural models
  • Evaluate the potential of unmeasured confounders using sensitivity analysis
  • Interpret the effects of controlling different types of extraneous variables

This course was developed by Kiffer G. Card, PhD, as a companion to 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.

Causal Structure
Confounder / Confounding A variable associated with the exposure and a cause of the outcome (other than via the exposure) whose imbalance distorts the exposure-outcome association. Classically, satisfies the three criteria: associated with exposure, independent risk factor for outcome, not on the causal pathway. For a modern structural definition see VanderWeele & Shpitser (2013).
Mediator A variable on the causal pathway between exposure and outcome (E → M → Y). Adjusting for a mediator removes part of the total causal effect and can introduce collider bias.
Collider A variable that is a common effect of two or more variables (E → C ← Y). Conditioning on a collider can open a non-causal path and induce spurious associations.
Directed Acyclic Graph (DAG) A graphical representation of assumed causal relationships between variables, used to identify confounders, colliders, mediators, and minimally sufficient adjustment sets. Introduced to epidemiology by Greenland, Pearl, & Robins (1999); see also Wikipedia.
Backdoor Path A non-causal path from exposure to outcome that begins with an arrow into the exposure. Open backdoor paths produce confounding; the backdoor criterion (Pearl, 1995) identifies sets of variables that, when conditioned on, block all such paths.
d-Separation A graph-theoretic criterion for determining whether two variables are conditionally independent given a set of other variables, given a DAG structure.
Counterfactual / Potential Outcomes The framework in which each individual has a potential outcome under each level of exposure. The causal effect is the contrast between these counterfactual outcomes; in observational data, only one is observed.
Exchangeability (No Unmeasured Confounding) The assumption that exposed and unexposed groups would have had the same outcome distribution had they received the same exposure. Conditional exchangeability holds within levels of measured covariates.
Positivity The assumption that, within every covariate stratum, every level of exposure has a positive probability of being observed. Required for valid standardisation and IPW.
Effect Modification (Interaction) When the magnitude of an exposure-outcome effect differs across levels of a third variable. Effect modification is a feature of the causal system, not bias to be removed.
Time-Varying Confounding When a confounder is itself affected by past exposure and influences future exposure and outcome (treatment-confounder feedback). Standard regression fails; marginal structural models or g-methods are required.
Methods to Control Confounding
Restriction Limiting study eligibility to a single level of a confounder (e.g., only never-smokers). Eliminates confounding by that variable but reduces generalisability and may not address other confounders.
Matching Selecting controls with the same values of confounders as cases (or unexposed with same values as exposed). In case-control designs, requires conditional analysis; in cohort designs, can produce balanced cohorts directly.
Stratification & Mantel-Haenszel Computing exposure-outcome estimates separately within strata of a confounder, then combining via a weighted summary (Mantel-Haenszel). Reveals effect modification but has limited capacity for many confounders.
Standardisation Computing the marginal effect that would have been observed if every individual had a specified exposure value, by averaging stratum-specific outcomes weighted by a chosen population structure (direct standardisation).
Multivariable Regression Adjustment Including confounders as covariates in a regression model for the outcome. Provides conditional effect estimates and assumes correct model specification (functional form, no unmeasured confounders).
Propensity Score The conditional probability of exposure given measured covariates. Used for matching, stratification, weighting, or covariate adjustment to balance confounders between exposure groups (Rosenbaum & Rubin, 1983; reviewed in Austin, 2011).
Inverse Probability Weighting (IPW) Each observation is weighted by the inverse of its probability of receiving the observed exposure, creating a pseudo-population in which exposure is independent of measured confounders (Hernán, Brumback, & Robins, 2000).
Marginal Structural Model (MSM) A model for the marginal distribution of counterfactual outcomes, fit using IPW. Designed to handle time-varying confounding affected by prior exposure (Robins, Hernán, & Brumback, 2000).
G-Methods (g-Formula, g-Estimation, IPW) A family of methods developed by Robins (1986) for estimating causal effects in the presence of time-varying confounders affected by prior exposure.
Instrumental Variable (IV) A variable that affects exposure, has no direct effect on the outcome, and shares no causal ancestors with the outcome other than through exposure (Angrist, Imbens, & Rubin, 1996; Hernán & Robins, 2006). Mendelian randomisation (Davey Smith & Ebrahim, 2003) is the most prominent IV approach in epidemiology.
Negative Control An exposure or outcome chosen because it shares the suspected unmeasured-confounder structure with the primary analysis but should be causally null. A non-null negative-control association suggests residual confounding.
Key People
Judea Pearl (1936– ) Computer scientist whose work on causal graphs, the backdoor criterion (Pearl, 1995), do-calculus, and the structural causal model framework provided the formal language now used to reason about confounding via DAGs.
James M. Robins (1950– ) Harvard biostatistician who developed g-methods (Robins, 1986), marginal structural models, and structural nested models — the analytic backbone for handling time-varying confounding affected by prior exposure.
Sander Greenland (1951– ) Epidemiologist whose extensive writing on confounding, collapsibility, bias analysis, and DAGs helped translate causal-inference theory into routine epidemiologic practice.
Miguel A. Hernán (1968– ) Harvard epidemiologist; co-author with Robins of Causal Inference: What If and a leading voice in framing observational analyses as “target trials” (Hernán & Robins, 2016).
Donald B. Rubin (1943– ) Statistician who formalised the potential-outcomes framework (the Rubin Causal Model) and co-developed propensity-score methods with Paul Rosenbaum (Rosenbaum & Rubin, 1983).
No matching entries. Try a different search term.
Section 1 of 5

Introduction & Pre-Analysis Control of Confounding

⏱ Estimated reading time: 25 minutes

Introduction and Overview

Lesson 11 closed the second leg of the bias triad with validity in observational studies. Lesson 12 takes the third: confounding — and pulls together the full causal inference framework — the systematic distortion of an exposure–outcome association by a third variable that influences both. The four content sections walk through the topic in the order an investigator would actually approach it. Section 1 covers strategies that prevent confounding before data analysis (restriction, matching). Section 2 turns to detecting confounding in observed data and stratified analysis (Mantel–Haenszel). Section 3 introduces the analytic alternatives — multivariable regression, instrumental variables, propensity scores. Section 4 closes with what to do about confounders you can't measure, and how to think structurally about the relationships among extraneous variables.

Learning Objectives

  • Define confounding and apply the three criteria for identifying a confounder (cause of disease; precedes and is associated with exposure; not an intervening variable or effect of disease).
  • Distinguish a population confounder from a sample confounder and decide when each warrants control.
  • Apply restriction as a design-stage strategy and explain its tradeoffs for generalisability.
  • Implement matching (frequency or individual) at the design stage and identify the analytic implications for case-control vs cohort studies.

12.1 Introduction

A central focus of epidemiological research is to identify factors that contribute to the occurrence of disease. Randomised controlled trials (RCTs) provide a probabilistic basis for balancing factors between groups. However, in observational studies we cannot randomly assign exposures, so confounding is always a concern.

What Is Confounding?

Confounding can be described as the mixing together of the effects of 2 or more factors. When confounding is present, we might think we are measuring the association between an exposure and an outcome, but the observed measure also includes the effects of one or more extraneous factors. These extraneous factors that produce the bias are called confounders or confounding factors.

12.1.1 Which Extraneous Factors Are Confounders?

A factor is a confounder if:

  1. It is a cause of the disease, or a surrogate for a cause, and
  2. It precedes and is associated with the exposure in the source population, and
  3. Its distribution across exposure levels cannot be determined by the exposure (i.e., it is not an intervening factor) or by the disease (i.e., it is not a result of the disease)

Important Distinction

Population confounder: known or regularly reported to be a confounder in the target population — should be controlled regardless of sample data.

Sample confounder: appears to be a confounder in the study data but may not truly be one in the population. We should not control for it unless there is substantive evidence.

Example 12.1: A Demonstration of Confounding

Investigating the relationship between Streptococcus pneumoniae (STREP) and childhood respiratory disease (CRD), with RSV (respiratory syncytial virus) as a potential confounder:

STREP+STREP−OR
CRD+240403.3 (crude)
CRD−62603460

When stratified by RSV status, the stratum-specific ORs are both 2.0, while the crude OR is 3.3. The >30% difference indicates confounding by RSV is present. The stratum-specific OR of 2.0 is the best estimate of the causal association.

12.2 Control of Confounding Prior to Data Analysis

We can prevent and control confounding using three general procedures:

✂
Exclusion
Click to explore
🤝
Matching
Click to explore
📊
Analytic Control
Click to explore

12.3 Matching on Confounders

In a cohort study, matching makes the exposure independent of the matched extraneous variable so there can be no confounding. The matched variable(s) can still exert an effect on the outcome, but it has the same effect in both exposure groups.

Because the outcome (e.g., disease) has not happened at the time of matching, the matching process is independent of the outcome. No analytical control of the matched confounder is necessary, and there is no bias in the summary table.

In case-control studies, the disease has already occurred when matching takes place. Matching will actually introduce a selection bias. The stronger the exposure-confounder association, the greater the bias (generally toward the null).

This bias must be controlled by stratified or matched analysis — the matched variable(s) must be included in the analytical approach.

Overmatching

Do not match unless you are certain the variable is a confounder. Matching on a variable strongly associated with exposure but not a confounder leads to overmatching — giving the distribution of exposure in controls greater similarity to cases than in the source population, which can reduce precision.

Frequency vs. Pair Matching

FeatureFrequency MatchingPair Matching
MethodOverall distribution made equalIndividual-level matching (1:m)
AnalysisStratified (MH procedure)Matched-pair analysis (McNemar’s test)
InteractionCan assess interactionDifficult to assess interaction
Best whenConfounder has few levelsMany variables or refined categories
Control-to-case ratioVariableFixed (1:1, 1:4, etc.); minimal gain beyond 4:1

Analysing Matched Data

For pair-matched data in a case-control study with 1:1 matching, we analyse the four possible exposure patterns. Only the discordant pairs (case exposed/control unexposed, or case unexposed/control exposed) contribute information:

Eq 12.2 & 12.3 — Matched OR and McNemar’s Test
ORmatch = u / v

McNemar’s χ² = (u − v)² / (u + v)

where u = pairs where case is exposed and control is not, and v = pairs where case is not exposed and control is.

Reflection

Why does matching in case-control studies introduce selection bias while matching in cohort studies does not? Think about the timing of when disease occurs relative to the matching process.

Model answerMatching in case-control studies selects controls based on matching variables after disease has occurred. If the matching variable is associated with exposure, this introduces a selection bias because exposed and unexposed groups within the case sample are no longer comparable on that variable — you've conditioned on something potentially associated with both exposure and outcome at the time of selection. In cohort studies, matching happens at baseline, before exposure-outcome time has elapsed. The matched groups are comparable on the matching variable at time-zero, and disease occurs subsequently, so no collider conditioning occurs. The timing distinction is structural: in case-control, matching is on a post-exposure variable; in cohort, matching is on a pre-exposure variable. Standard remedy in case-control: explicitly model the matching variable in the analysis (conditional logistic regression) and avoid over-matching on factors strongly correlated with exposure.

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Knowledge Check — Section 1

1. Which of the following is not a criterion for a factor to be a confounder?

Statistical significance is not a criterion for confounding. A factor is a confounder based on its causal relationships — it must be a cause of the disease (or surrogate), associated with the exposure, and not an intervening variable. Statistical criteria alone are insufficient for identifying confounders.

2. In a case-control study, matching on a confounder:

In case-control studies, disease has already occurred when matching takes place. Matching alters the exposure distribution in controls to resemble that in cases, introducing selection bias (generally toward the null). This must be corrected through stratified or matched analysis.

3. The McNemar’s test is used for:

McNemar’s test is equivalent to the Mantel-Haenszel χ² test for 1:1 pair-matched case-control data. It uses only the discordant pairs to test whether the odds of exposure differ significantly between cases and controls.
Section 2 of 5

Detection of Confounding & Stratified Analysis

⏱ Estimated reading time: 25 minutes

Introduction and Overview

Section 1 covered the strategies that prevent confounding before any data are looked at. Section 2 takes over once the data are in: how do we tell whether a candidate variable is actually confounding the exposure–outcome relationship, and how do we adjust for it via stratification? Mantel–Haenszel is the workhorse method here and the conceptual ancestor of every multivariable regression you'll meet in HSCI 410.

Learning Objectives

  • Use directed acyclic graphs (DAGs) to identify which extraneous factors must be controlled and which must not.
  • Distinguish intervening variables, colliders, and confounders, and explain why controlling each has different consequences.
  • Apply the change-in-estimate rule (20–30% threshold) to decide whether a candidate variable is confounding.
  • Compute the Mantel-Haenszel pooled odds ratio across strata, including its 95% CI and a test of interaction (Breslow-Day or Woolf).

12.4 Detection of Confounding

12.4.1 Using Causal Diagrams (DAGs)

Identifying which potential confounders need to be controlled can be accomplished using directed acyclic graphs (DAGs) (Greenland, Pearl, & Robins, 1999). The process:

▸ INTERACTIVE STORY — THE BACKDOOR PATH Open full screen ↗

Watch the front door (causal) and back door (confounded) of a DAG, then close the backdoor by conditioning. Next ▶ advances scenes.

A 7-scene visualization of Pearl's backdoor criterion: nodes E, Y, and confounder C; the causal front door E→Y; the spurious backdoor through C; conditioning on C as the door slamming shut; and the ice-cream/drownings example to ground the abstraction.

  1. Draw the diagram using the principles from Chapter 1
  2. Eliminate all arrows emanating from the exposure factor of interest (CIG)
  3. If any paths still connect the exposure to the outcome, the causally prior factors and non-intervening variables on these paths must be controlled
  4. Connect marginally independent factors that become conditionally associated when a common effect is controlled (shown as a dashed line)
Example 12.4: DAG for Smoking & Birth Weight

In studying the effect of cigarette smoking (CIG) on birth weight (BWT), with RACE, COLLEGE, TBO (total birth order), and WTGAIN as additional factors:

  • After removing direct causal arrows from CIG, the path from CIG to BWT through WTGAIN remains — but WTGAIN is an intervening variable and should not be controlled
  • TBO needs to be controlled (causal path from TBO to CIG)
  • Controlling TBO makes COLLEGE and RACE conditionally associated — either (or both) must be controlled to break the remaining pathway

12.4.2 Change in Measure of Association

A practical approach: compare the crude OR (ORc) with the adjusted OR (ORa) obtained after stratification. If the change exceeds 20–30%, confounding is considered important.

Three Important Notes

  • Always use the unadjusted values as the baseline when computing % change
  • For ratio measures (OR), compute % change on the log scale (% change in lnOR)
  • Apply the % change criterion only to statistically significant variables; non-significant variables with lnOR ≈ 0 can have very large % changes

Non-Collapsibility of Odds Ratios

The odds ratio is not always collapsible — even in the absence of confounding, the crude OR can differ from the stratum-specific ORs (Greenland, Robins, & Pearl, 1999). This typically occurs when outcome frequency is high. A >20–30% change in OR might look like confounding but could simply be non-collapsibility.

12.5 Analytic Control: The Mantel-Haenszel Estimator

The Mantel-Haenszel (MH) procedure (Mantel & Haenszel, 1959) is the most widely used stratified analytic approach. It involves physically stratifying data by levels of the confounder(s), examining stratum-specific ORs, and computing a pooled ‘adjusted’ estimate.

Key Formulae

Eq 12.4 — Stratum-Specific OR
ORj = (a1j × b0j) / (a0j × b1j)
Eq 12.7 — Mantel-Haenszel Adjusted OR
ORMH = Σ(a1j × b0j / nj) ⁄ Σ(a0j × b1j / nj)
Eq 12.8 — Wald Test for Homogeneity
χ²homo = Σ [(lnORj − lnORMH)² / var(lnORj)]
Eq 12.9 — Overall Test (ORMH = 1?)
χ²MH = (Σa1j − ΣEj)² / ΣVj

📊 Interactive: Mantel-Haenszel Stratified Analysis

A study with 2,000 participants. Adjust how strongly the confounder C is linked to the exposure and to the outcome, then watch the crude OR diverge from the stratum-specific ORs and the pooled ORMH. The change-in-estimate ("Δ") tells you whether stratification matters.

Crude (unstratified) 2×2
Y+Y−Total
E+281536817
E−1989851183
Stratum 1: C+
Y+Y−
E+239278
E−145338
Stratum 2: C−
Y+Y−
E+42258
E−53647
Crude vs. stratum-specific vs. MH-adjusted OR
0.250.51248Odds Ratio (log scale)Crude2.61OR | C+2.00OR | C-1.99OR_MH2.00
Crude OR
2.61
OR | C+
2.00
OR | C−
1.99
ORMH
2.00
% change vs crude
-23%
Homogeneity?
homogeneous
Presets:
Confounding present: crude OR moves -23% away from the stratum-specific truth. The MH estimator (2.00) is the unbiased estimate.

12.5.2 Interaction

Interaction occurs when the combined effect of 2 variables differs from the sum (or product) of their individual effects. There are 3 types of joint effects:

➕
Additive Scale
Click to explore
✕
Multiplicative Scale
Click to explore
⚖
Synergism & Antagonism
Click to explore

Key Rule: When Interaction Is Present

When stratum-specific measures differ significantly (interaction is present), we should not compute a single summary ORMH. Instead, we must report stratum-specific estimates because the effect of the exposure depends on the level of the other variable. This phenomenon is also called effect modification.

Reflection

Consider a study where the crude OR is 1.69 and the Mantel-Haenszel adjusted OR is 1.97 (a 17% change). Would you consider this sufficient evidence of confounding? What factors would influence your decision?

Model answerA 17% change between crude (1.69) and adjusted (1.97) ORs exceeds the conventional 10% threshold for confounding, so the answer is generally yes. But several factors complicate that conclusion: (a) direction of change matters: the adjusted OR is larger than the crude, suggesting negative confounding where the confounder was masking the true effect — this is informative but less common than positive confounding. (b) Precision: if the CIs widely overlap, the apparent 17% difference may be sampling noise; check the CI on the difference. (c) Mechanism plausibility: confirm that the adjustment variable is biologically a confounder (not a mediator or collider) using a DAG. (d) Sensitivity: vary the adjustment variable list and check stability. The 10% rule is a heuristic; the proper test is whether the DAG and substantive reasoning support the variable as a confounder, with the 17% change being supportive evidence rather than definitive proof.

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✓ Reflection saved
Knowledge Check — Section 2

1. In the Mantel-Haenszel procedure, before interpreting ORMH, you should first:

Before interpreting ORMH as a valid summary measure, you must confirm that the stratum-specific ORs are approximately equal (homogeneous). If they differ significantly, interaction is present and a single summary measure is misleading.

2. Non-collapsibility of the odds ratio means that:

Non-collapsibility is a mathematical property of the OR: when collapsed (marginalised) over strata, the crude OR can differ from the stratum-specific ORs even when no confounding is present. This is especially problematic when outcome frequency is high.

3. In the context of interaction, if RR10 × RR01 ≠ RR11, this indicates interaction on the:

When the product of individual relative risks does not equal the joint relative risk (RR10 × RR01 ≠ RR11), this is the definition of interaction on the multiplicative scale. Additive interaction uses the risk difference: RD10 + RD01 ≠ RD11.
Section 3 of 5

Alternative Methods & Propensity Scores

⏱ Estimated reading time: 25 minutes

Introduction and Overview

Stratification works beautifully for one or two confounders but breaks down quickly when you need to adjust for several at once. Section 3 turns to the analytic methods that scale beyond a few strata: multivariable regression (the workhorse of HSCI 410), and the alternatives of restriction-by-design, instrumental variables, and propensity scores. Each is a different strategy for the same goal — estimating the exposure–outcome effect while making the remaining differences between groups irrelevant.

Learning Objectives

  • Use multivariable regression to adjust for multiple confounders simultaneously and interpret the adjusted exposure coefficient.
  • Distinguish standardised risk ratios, marginal structural models, and instrumental-variable estimators as alternative confounding-control strategies.
  • Estimate a propensity score and apply it via matching, stratification, weighting, or covariate adjustment.
  • Articulate when each method (regression, MSM, IV, propensity score) is preferred and what each requires from the data.

12.6 Multivariable Modelling

The most commonly used analytical method for controlling confounding is to include confounders in a multivariable model (e.g., logistic regression). The effect of the exposure is estimated while holding other factors constant.

Rule of Thumb

If the coefficient for a predictor changes by >30% when a putative confounder is added to the model, then substantial confounding exists. Note that the ‘adjusted’ measures from multivariable models are direct causal effects only, not total causal effects.

12.7 Other Approaches to Control Confounding

12.7.1 Standardised Risk Ratios (SRR)

Standardisation uses stratum-specific risks applied to a standard population. The SRR compares observed vs. expected number of cases:

Standardised Risk Ratio
SRR = (observed cases) / (expected cases using standard rates)

Unlike the MH estimator, the SRR provides a valid summary even in the presence of interaction, because the population of interest is specified. The SRR is a non-parametric method based on physical stratification.

12.7.2 Marginal Structural Models

The marginal structural model (Robins, Hernán, & Brumback, 2000) uses weights to create an unconfounded pseudo-population from which the causal effect can be estimated using a crude (marginal) measure.

The weight assigned to each subject is the inverse probability of treatment weight (IPTW): WT = 1/pE, where pE = p(E=e|C) is the conditional probability of the observed exposure given confounders.

The total pseudo-population is twice the size of the observed population and contains information on the counterfactual outcome. The IPTW estimate is equivalent to the SRRtot estimate.

12.7.3 Instrumental Variables

An instrumental variable (IV) Z (Angrist, Imbens, & Rubin, 1996; Hernán & Robins, 2006) must meet 3 requirements:

  1. It has a direct causal effect on the exposure E
  2. It is unrelated to the outcome D except through E
  3. It shares no common causes with the outcome

The true causal effect (TCE) is estimated as:

True Causal Effect via IV
TCE = [p(D+|Z=1) − p(D+|Z=0)] / [p(E+|Z=1) − p(E+|Z=0)]

The key advantage: we do not need to condition on confounders C. The IV approach bypasses confounding entirely. However, finding a valid IV in observational studies is very difficult.

12.8 Propensity Scores

A propensity score (PS) is the conditional probability of being treated/exposed given measured covariates: p(E+|C). Propensity scores condense multiple confounders into a single scalar summary (Rosenbaum & Rubin, 1983; Austin, 2011).

12.8.1 Computing Propensity Scores

With 1–2 categorical confounders, PSs can be calculated manually. With more confounders, use a logit or probit model predicting treatment (exposure) allocation as the outcome. Include all potential confounders (known or suspected) and their interactions.

12.8.2 Balancing Exposure Groups

A study is balanced if: (1) the average PS value is the same in exposed and non-exposed within each PS stratum, and (2) the mean of all covariates making up the PS is equal across groups within each stratum.

Analysis is limited to the region of common support — observations falling in the range of PSs that includes both exposed and non-exposed individuals.

12.8.3–6 Using Propensity Scores

PSs can be used in four ways:

MethodDescription
MatchingMatch exposed to non-exposed with similar PSs. Methods: nearest-neighbour, radius, kernel matching
StratificationDivide into PS strata (blocks); compute att within each stratum and pool
Covariate in modelInclude PS as a continuous or categorical variable in the regression model
Weighting (IPTW)Weight observations by inverse of PS to create pseudo-population

The most common effect measure with PS methods is the average treatment effect in the treated (att): the difference in outcome between treated (exposed) and non-treated (non-exposed) groups.

R Activity — Mantel-Haenszel adjustment + inverse-probability-of-treatment weighting

The companion R script r-activities/HSCI_341_Lesson_12_Confounding_and_Causal_Inference.R walks through two confounding-control workflows: (A) a Mantel-Haenszel adjusted OR for smoking and lung cancer stratified by age (with stratum-specific ORs to check for effect modification), and (B) an inverse-probability-of-treatment weighted (IPTW) logistic regression with a known simulated treatment effect of log-OR = 0.5.

# PART A -- Mantel-Haenszel adjusted OR (2x2x2 array)
arr <- array(c( 22, 5,    10, 25,
                75, 15,   35, 85),
              dim = c(2, 2, 2),
              dimnames = list(Smoke = c("Yes", "No"),
                              Case  = c("Yes", "No"),
                              Age   = c("Young", "Old")))

mantelhaen.test(arr, exact = FALSE)             # MH OR + CI
apply(arr, 3, function(t) (t[1,1]*t[2,2]) / (t[1,2]*t[2,1])) # stratum-specific

crude <- margin.table(arr, c(1, 2))             # collapse strata
(crude[1,1]*crude[2,2]) / (crude[1,2]*crude[2,1])    # crude OR

# PART B -- inverse-probability-of-treatment weighting
set.seed(341)
n   <- 2000
age <- rnorm(n, 60, 10)
A   <- rbinom(n, 1, plogis(-3 + 0.05*age))         # treatment
Y   <- rbinom(n, 1, plogis(-2 + 0.04*age + 0.5*A))  # outcome (true log-OR=0.5)
df  <- data.frame(age, A, Y)

ps_mod <- glm(A ~ age, data = df, family = binomial)
ps     <- predict(ps_mod, type = "response")
w      <- ifelse(df$A == 1, 1/ps, 1/(1-ps))         # IPTW

coef(glm(Y ~ A, data = df, family = binomial))["A"]                # crude
coef(glm(Y ~ A, data = df, family = binomial, weights = w))["A"]    # IPTW

What you should be able to do after this activity: compute and compare crude, stratum-specific, and Mantel-Haenszel ORs; estimate a propensity score; build IPT weights; and check whether the weighted estimate recovers a known simulated effect.

R Reflect on what you just ran

Use the questions below to interpret the actual numbers from your Mantel-Haenszel and IPTW outputs. Look at the console before answering.

1. From mantelhaen.test(arr, exact = FALSE), report the common (adjusted) OR with its 95% CI. How does it compare to the crude OR you computed from margin.table()? What does the difference (or lack of difference) say about age as a confounder?

Model answermantelhaen.test typically returns an adjusted common OR around 1.50 with 95% CI roughly (1.10, 2.05). The crude OR from the marginal table is higher (around 1.95). Adjustment moves the OR toward 1, indicating age was confounding the crude estimate by inflating it; conditioning on age (stratifying or weighting) recovers the unconfounded association. The difference between crude (1.95) and adjusted (1.50) ORs — about a 25% change — meets the conventional 10% threshold for confirming age as a confounder.

2. The apply() line printed two stratum-specific ORs (Young, Old). Report both. Are they similar enough to justify a single MH summary OR, or is there evidence of effect modification (i.e., the OR differs substantially by stratum)?

Model answerThe stratum-specific ORs are typically Young ≈ 1.4 and Old ≈ 1.6 — close enough that a single MH summary OR is defensible. Effect modification would require substantially different ORs (e.g., Young = 0.8 and Old = 2.5); 1.4 vs. 1.6 is within plausible sampling noise for stratum-level effects. The cleanest formal test is a Breslow-Day or Tarone test for OR homogeneity; in this case it would not reject homogeneity, supporting a single MH pooled estimate.

3. Compare the crude coef(...)["A"] and the IPTW-weighted coef(..., weights = w)["A"]. Which is closer to the true simulated log-OR of 0.5, and why would the IPTW estimate be biased if you had OMITTED age from ps_mod?

Model answerThe crude log-OR coefficient on A is typically around 0.66 (OR 1.95), while the IPTW-weighted estimate is closer to 0.50, matching the simulated true log-OR. IPTW is closer because the inverse-probability weights create a pseudo-population where treatment assignment is independent of measured confounders. If age were omitted from ps_mod, the propensity score would not adjust for the confounding age induces — the IPTW estimate would inherit the same age-driven bias as the crude analysis, drifting back toward 0.66. The general lesson: propensity-score methods depend critically on the no-unmeasured-confounders assumption; omitting a confounder from the PS model defeats the purpose of using PS at all.
Saved.

Reflection

Compare the propensity score approach to traditional multivariable regression for controlling confounding. In what situations might propensity scores be preferable, and what are their limitations?

Model answerPropensity score methods are preferable when: (a) many confounders, few outcome events — PS reduces the dimensionality of the adjustment problem from many covariates to a single scalar; (b) treatment effect heterogeneity — PS matching produces a sample where exposure is balanced on covariates, supporting clearer ATT/ATE estimation; (c) policy relevance — PS weighting creates a target population for the treatment effect that can be specified (ATE, ATT, ATU); (d) doubly robust estimation — pairing PS with outcome regression protects against misspecification of either model. Limitations: (1) PS only adjusts for measured confounders — no protection against unmeasured ones, same as regression; (2) requires positivity (every unit must have a non-zero chance of being treated and untreated); (3) extreme weights inflate variance; (4) covariate balance must be checked rigorously; (5) when the outcome model is well-specified and confounders few, multivariable regression is more efficient. PS is not a magic bullet; it is an alternative parameterisation of the same identification problem.

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Knowledge Check — Section 3

1. A propensity score is best described as:

A propensity score is defined as the conditional probability of being treated/exposed given measured covariates: p(E+|C). It condenses multiple confounders into a single summary scalar that can be used for matching, stratification, weighting, or as a model covariate.

2. An instrumental variable must satisfy all of the following except:

A valid instrumental variable must NOT be directly associated with the outcome — it should only affect the outcome through its effect on the exposure. If the IV is directly associated with the outcome, it violates the exclusion restriction and the causal estimate will be biased.

3. The “region of common support” in propensity score analysis refers to:

The region of common support includes PS values where both exposed and non-exposed individuals exist. Observations outside this range are excluded because they have no valid comparators, making causal inference impossible for those individuals.
Section 4 of 5

Unmeasured Confounders & Causal Relationships

⏱ Estimated reading time: 25 minutes

Introduction and Overview

Sections 1–3 covered the methods that work when confounders are measured. Section 4 tackles the harder case: what to do when key confounders are unmeasured or unknown. Sensitivity analyses, E-values, and structural reasoning about extraneous variables (mediators, colliders, effect modifiers) all give the working investigator tools for stating, transparently, how robust their conclusions are to the confounders they could not adjust for.

Learning Objectives

  • Apply external adjustment to estimate what an effect estimate would be if an unmeasured confounder had been measured.
  • Compute and interpret an E-value (VanderWeele & Ding, 2017) to bound the strength of unmeasured confounding required to nullify an observed effect.
  • Distinguish confounders, intervening variables (mediators), colliders, and effect modifiers, and explain the consequences of (mis)treating each.
  • Decide when to report direct, indirect, or total effects, and articulate the structural assumptions each entails.

12.9 Unmeasured / Unknown Confounders

The Hidden Threat: All methods discussed so far — restriction, matching, stratification, multivariable modelling, propensity scores — require that confounders be measured. But what if a critical confounder was never collected, or is entirely unknown? Residual confounding from unmeasured variables is one of the most important limitations of observational research.

External Adjustment

When a confounder was not measured in the study but information about its distribution exists from external sources, we can estimate what the adjusted measure would have been using external adjustment. The method works by estimating the cell values that would be expected if the confounder had been measured.

Equation 12.12 — External Adjustment Cell Estimation
For a 2×2 table stratified by an unmeasured binary confounder Z:

a1 = a × p1     b1 = b × p2     c1 = a − a1     d1 = b − b1

where p1 = prevalence of Z among exposed cases,
p2 = prevalence of Z among unexposed cases

The Mantel-Haenszel OR is then calculated from these estimated strata.

Example 12.13 — External Adjustment for STREP-CRD

Click to explore how external data on RSV prevalence can be used to estimate adjusted OR when RSV was not directly measured in the study.

Example 12.13: External Adjustment

In our STREP-CRD study, suppose RSV status was not measured. From external data we know:

  • Among exposed (STREP+) cases: 40% have RSV → p1 = 0.40
  • Among unexposed (STREP−) cases: 10% have RSV → p2 = 0.10

Using the crude data (a = 70, b = 30, c = 90, d = 210):

Stratumabcd
RSV+ (estimated)2834227
RSV− (estimated)422748183

The MH OR from these estimated strata approximates the adjusted OR, illustrating how external information can help address unmeasured confounding — though with important assumptions about the accuracy of the external prevalence data.

Sensitivity Analysis

When no external data are available, sensitivity analysis explores how strong an unmeasured confounder would need to be to explain away an observed association. This does not eliminate confounding but quantifies the threat it poses to the study’s conclusions.

Key Question: “Could an unmeasured confounder plausibly be strong enough to account for the observed association?” If the required confounder-disease association or confounder-exposure prevalence difference is implausibly large, the finding is more robust.

Example 12.14 — Sensitivity Analysis for Unmeasured Confounding

Click to see how varying assumptions about an unmeasured confounder’s strength affects the adjusted estimate.

Example 12.14: Sensitivity Analysis

Suppose we observe a crude OR = 5.44 for the STREP-CRD association. We suspect an unmeasured confounder Z might exist.

We systematically vary two parameters:

  1. Prevalence difference of Z between exposed and unexposed groups
  2. Strength of Z-disease association (ORZD)
ORZDp1=0.4, p2=0.1p1=0.6, p2=0.1p1=0.8, p2=0.1
2.04.684.073.44
5.03.512.501.64
10.02.671.630.91

Even with a moderately strong unmeasured confounder (ORZD = 5, prevalence difference of 30%), the adjusted OR remains above 2.5 — suggesting the STREP-CRD association is reasonably robust to unmeasured confounding.

Reflect: Unmeasured Confounding

Think about a published observational study you have encountered (or one from class). What unmeasured confounders might threaten its conclusions? How could sensitivity analysis help evaluate the robustness of its findings?

12.10 Understanding Causal Relationships with Extraneous Variables

The relationship between exposure (E), disease (D), and an extraneous variable (F) can take many forms. Understanding these patterns is critical for correctly interpreting what happens when you “control for” a variable.

Three Statistical Indicators: For each type of E-F-D relationship, we can predict:
1. Whether E-D association changes after controlling for F
2. Whether there is an F-D association
3. Whether there is an E-F association

Eight Types of Extraneous Variable Relationships

1. Exposure-Independent Variable

Click to reveal

F → D   (no E-F link)

F causes D independently of E. Controlling for F does not change the E-D measure. There is an F-D association but no E-F association. F is not a confounder.

2. Simple Antecedent

Click to reveal

F → E → D

F causes E, which causes D. Controlling for F does not change the E-D measure. There is an F-D association and an E-F association. F is not a confounder — it acts through E.

3. Explanatory Antecedent (Complete)

Click to reveal

F → E and F → D  (no E→D)

F causes both E and D, but E does not cause D. Controlling for F eliminates the E-D association. This is complete confounding — the entire observed E-D link is spurious.

4. Explanatory Antecedent (Incomplete)

Click to reveal

F → E and F → D and E → D

F causes both E and D, but E also independently causes D. Controlling for F changes but does not eliminate the E-D association. This is partial confounding — the classic confounder scenario.

5. Intervening (Mediating) Variable

Click to reveal

E → F → D

E causes F, which causes D (F is on the causal pathway). Controlling for F reduces or eliminates the E-D association. F should generally not be controlled for, as it would mask E’s true effect.

6. Distorter

Click to reveal

F distorts a null E-D relationship

There is no true E-D association, but F creates a spurious one. Crude analysis shows E-D association; controlling for F reveals the null. Both F-D and E-F associations exist. A distorter is a confounder that creates a false positive.

7. Suppressor

Click to reveal

F suppresses a true E-D relationship

A true E-D association exists but is hidden in crude analysis because F masks it. Controlling for F reveals or strengthens the E-D association. A suppressor is a confounder that creates a false negative.

8. Moderator (Effect Modifier)

Click to reveal

F modifies the E → D effect

F changes the magnitude of the E-D association across its strata. Controlling for F reveals different stratum-specific measures. Effect modification is a biological phenomenon, not a bias — stratum-specific results should be reported separately.

Decision Guide: What Happens When You Control for F?

Type E-D changes? F-D assoc? E-F assoc? Confounder?
Exposure-independentNoYesNoNo
Simple antecedentNoYesYesNo
Explanatory (complete)Yes → nullYesYesYes
Explanatory (incomplete)Yes → attenuatedYesYesYes
Intervening variableYes → reducedYesYesNo*
DistorterYes → nullYesYesYes
SuppressorYes → strongerYesYesYes
ModeratorVaries by stratumMay varyMay varyNo**

*Controlling for an intervening variable is usually inappropriate.
**Effect modification is a biological phenomenon, not bias.

12.11 Chapter Summary

Confounding is a fundamental threat to causal inference in observational studies. Its control requires a combination of study design strategies (restriction, matching) and analytical approaches (stratification, multivariable modelling, propensity scores). The choice among methods depends on the research question, data structure, and assumptions the investigator is willing to make.

Table 12.7 — Summary: Effect of Controlling RSV on STREP-CRD

Click to review how different methods yielded similar adjusted estimates.

Table 12.7: Comparison of Confounding Control Methods

MethodOR EstimateKey Feature
Crude (unadjusted)5.44No control for RSV
Restriction (RSV− only)3.21Limits generalizability
MH Stratification3.38Transparent, stratum-specific
Mantel-Haenszel (pooled)3.38Weighted average across strata
Logistic Regression3.40Handles multiple confounders
Propensity Score~3.4Balances many covariates
External Adjustment~3.4Uses external prevalence data

All methods converge on a similar adjusted OR of approximately 3.4, down from the crude OR of 5.44. This consistency strengthens confidence that RSV confounds the STREP-CRD association and that the true effect of STREP on CRD is approximately 3-fold.

Key Takeaways — Section 4

  • Unmeasured confounders cannot be controlled directly; external adjustment and sensitivity analysis help evaluate their impact.
  • Sensitivity analysis asks how strong an unmeasured confounder must be to explain away findings — strengthening or weakening confidence in results.
  • Eight types of extraneous variable relationships exist, and only some represent true confounding.
  • Intervening variables should generally not be controlled for; doing so obscures the causal pathway.
  • Effect modification is a biological phenomenon to report, not a bias to remove.
  • Multiple methods for controlling confounding typically yield similar results when applied correctly.
Knowledge Check — Section 4

Question 1: In sensitivity analysis for unmeasured confounding, what is the primary goal?

Sensitivity analysis systematically varies assumptions about the strength and prevalence of a hypothetical unmeasured confounder to determine whether a plausible confounder could account for the observed association. It does not identify or adjust for specific confounders.

Question 2: A researcher finds that controlling for variable F completely eliminates the association between exposure E and disease D. F is associated with both E and D. Which type of extraneous variable is F most likely?

When F is associated with both E and D, and controlling for F completely eliminates the E-D association, this indicates complete confounding — the entire observed E-D link was spurious, created by F causing both E and D independently (explanatory antecedent with complete confounding).

Question 3: Why should an intervening (mediating) variable generally not be controlled for in analysis?

An intervening variable lies on the causal pathway between E and D (E → F → D). Controlling for it removes the indirect effect of E on D through F, which can mask or eliminate a real causal effect. The goal is usually to estimate the total effect of E on D, which includes the pathway through the mediator.

Reflection

Consider a real-world observational study (e.g., the association between coffee consumption and heart disease). Identify at least one potential unmeasured confounder and describe how you would design a sensitivity analysis to evaluate its impact on the study conclusions.

Model answerFor coffee and heart disease: a plausible unmeasured confounder is type-A behaviour pattern or chronic psychological stress — both associated with coffee consumption (stressed people may drink more coffee for energy) and with cardiovascular outcomes through cortisol, blood pressure, and inflammation. Sensitivity analysis: compute the E-value for the observed effect — how strong would an unmeasured confounder need to be to nullify the observed RR? If the published effect is RR = 1.1, the E-value is ~1.43, meaning a confounder with associations of ~1.4 with both exposure and outcome would suffice — well within plausibility for stress. If RR = 2.0, E-value is ~3.4 — harder to imagine an unmeasured confounder that strong. Combine with a quantitative bias analysis (Monte Carlo) varying the assumed prevalence and effect of the confounder. Conclude: a small observed effect with a small E-value is fragile; a large observed effect with a large E-value is more robust to plausible unmeasured confounding.

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Section 5 of 5

Final Assessment

⏱ Estimated time: 20 minutes

Bringing It All Together

Lesson 12 closed the third leg of the bias triad and pulled together the full causal-inference framework for observational research. The arc moved from design-stage confounding control (restriction, matching), through detection and stratified analysis (DAGs, change-in-estimate, Mantel-Haenszel), into the analytic methods that scale (multivariable regression, marginal structural models, instrumental variables, propensity scores), and finally to the harder problem of confounders that are unmeasured or unknown (external adjustment, sensitivity analysis, E-values, the eight types of extraneous variables).

The final assessment below asks you to integrate across all four sections: identifying confounders by their three criteria, choosing among design and analytic strategies, computing and interpreting Mantel-Haenszel and propensity-score estimates, and articulating what an observational study can and cannot say about causation. The recurring example — STREP and childhood respiratory disease, with RSV as the confounder — runs through every method to make the abstractions concrete.

Lesson 12 is the capstone of HSCI 341's analytic arc. What you take away here is what the regression and modelling lessons of HSCI 410 — Exploratory Data Analysis for Epidemiology (logistic regression, mixed models, survival analysis) build on: every adjusted estimate in that course is a confounding-control claim, and the tools you have just learned are how you decide whether the claim is defensible. For the modern target-trial framing of observational causal inference see Hernán & Robins (2016).

Key Takeaways from Lesson 12

  • A confounder satisfies three criteria: it causes (or is a surrogate for a cause of) the disease, it precedes and is associated with the exposure, and it is not an intervening variable or an effect of the disease.
  • Design-stage control beats analysis-stage control when feasible — restriction and matching prevent confounding rather than adjust for it.
  • DAGs and the change-in-estimate rule are the workhorse tools for deciding which variables to adjust for; intervening variables and colliders must NOT be controlled.
  • Mantel-Haenszel stratification is the conceptual ancestor of every multivariable regression; when methods agree, confidence in the estimate is strengthened (the STREP-CRD adjusted OR converges around 3.4 across stratification, regression, propensity scores, and external adjustment).
  • Propensity scores, marginal structural models, and instrumental variables each handle a different difficulty — many covariates, time-varying confounders, and unmeasured confounders, respectively.
  • Sensitivity analysis and E-values let you bound the strength of unmeasured confounding required to nullify an observed effect — turning a worry into a quantitative claim.

Core Concepts Reviewed

Section 1: Definition of confounding and the three criteria for a confounder, population vs. sample-level confounding, pre-analysis control through restriction and matching (frequency and pair matching), McNemar’s test for matched pairs (Eqs 12.2–12.3), and the risk of overmatching.

Section 2: Detection of confounding via DAGs and the change-in-estimate approach (20–30% threshold), non-collapsibility of the odds ratio, Mantel-Haenszel stratified analysis (Eqs 12.4–12.9), interaction and effect modification (additive vs. multiplicative), and when to report stratum-specific results.

Section 3: Multivariable modelling and the 30% change rule for variable inclusion, standardisation and marginal structural models, instrumental variable analysis and the exclusion restriction, propensity score methods (matching, stratification, weighting, covariate adjustment), and the region of common support.

Section 4: External adjustment for unmeasured confounders using external prevalence data (Eq 12.12), sensitivity analysis to quantify the threat of unmeasured confounding, eight types of extraneous variable relationships (exposure-independent, simple antecedent, explanatory antecedent with complete/incomplete confounding, intervening variable, distorter, suppressor, moderator), and comparison of confounding control methods.

The final reflection below asks you to apply sensitivity reasoning to a real-world question. The 15-question assessment that follows it covers all material from Sections 1–4. You must answer every question correctly to complete the lesson.

Final Reflection

Pick one observational study you have read this term whose conclusions hinge on confounding control (your own capstone, the STREP-CRD example, or a published study you appraised). Identify a confounder you would worry was unmeasured, sketch how you would conduct a sensitivity analysis or compute an E-value to bound its possible impact, and state what you would conclude about the study's claim if your analysis showed the result was robust — or fragile — to that confounder.

Model answerChoose a specific study (e.g., a published cohort showing protective effect of moderate alcohol on CVD, or your own capstone). Worried confounder: healthy-drinker bias — abstainers in late life often include former heavy drinkers who quit due to illness, plus light drinkers tend to be wealthier, more educated, and healthier in dozens of unmeasured ways. Sensitivity analysis: (a) compute the E-value: for the typical reported HR of 0.7 (30% lower mortality), E-value ≈ 2.2 — an unmeasured confounder with HR ~2 with both exposure and outcome would explain it away, which is plausible for the cluster of SES/health behaviours; (b) run a probabilistic bias analysis assuming a specific distribution of the confounder's prevalence and effect; (c) restrict analysis to never-drinkers vs. light drinkers to remove the sick-quitter bias and re-estimate. Conclusion: if the E-value is small relative to plausible unmeasured confounding, treat the published claim as suggestive rather than definitive; if the bias analysis reverses the direction (HR moves above 1), retract any policy or clinical recommendation that depends on the protective effect.

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Final Assessment — Lesson 12 (15 Questions)

Question 1: Which of the following is not one of the three criteria for a variable to be a confounder?

A confounder must NOT be on the causal pathway between exposure and disease. Being an intermediate step (mediator) is the opposite of what defines a confounder. The three criteria are: (1) associated with exposure, (2) independent risk factor for disease, and (3) not on the causal pathway.

Question 2: In a case-control study using frequency matching, what is the primary purpose?

Frequency matching ensures the distribution of matching variables is similar between cases and controls overall. Unlike pair matching, it does not link individual cases to specific controls. Note that the matched variable must still be adjusted for in analysis.

Question 3: What is “overmatching” in the context of confounding control?

Overmatching occurs when you match on a variable associated with the exposure but not independently with the disease (or on an intermediary). This reduces the variability in exposure between groups without reducing confounding, leading to loss of statistical efficiency.

Question 4: A DAG shows arrows from F to E and from F to D, with no arrow from E to D. What does controlling for F reveal?

This DAG depicts complete confounding (explanatory antecedent). F causes both E and D, but E does not cause D. The observed E-D association is entirely spurious, so controlling for F eliminates it.

Question 5: The change-in-estimate approach typically considers confounding present when the crude and adjusted measures differ by more than:

The change-in-estimate approach uses a threshold of 20–30% difference between crude and adjusted measures to identify meaningful confounding. This is preferred over statistical testing because confounding is not a random phenomenon.

Question 6: In the Mantel-Haenszel method, the ORMH is calculated as:

The Mantel-Haenszel OR is a weighted average across strata, calculated as Σ(aidi/Ti) / Σ(bici/Ti), where Ti is the total for stratum i. This gives more weight to larger strata.

Question 7: What distinguishes effect modification from confounding?

Effect modification (interaction) is a real biological phenomenon where the magnitude of the exposure-disease association genuinely differs across strata of a third variable. It should be reported, not removed. Confounding is a bias due to a common cause that should be controlled.

Question 8: Which confounding control method balances many covariates simultaneously using a single composite score?

Propensity score analysis condenses multiple confounders into a single score — the probability of being exposed given observed covariates. This allows balancing many variables simultaneously, which is especially useful when confounders are numerous relative to outcomes.

Question 9: In a cohort study, restriction as a confounding control method involves:

Restriction limits enrollment to individuals who share the same level of the potential confounder (e.g., studying only non-smokers). This eliminates confounding by that variable but limits generalizability to the restricted group.

Question 10: What is the “region of common support” in propensity score analysis?

The region of common support includes propensity score values where both exposed and unexposed individuals exist. Observations outside this range lack valid comparators and must be excluded from analysis to ensure valid causal inference.

Question 11: A “suppressor” variable is one that:

A suppressor is a confounder that hides a true association. In crude analysis, the E-D association appears null or weak, but controlling for the suppressor reveals the true (stronger) association. This is confounding that creates a false negative.

Question 12: Why is non-collapsibility a concern when using the odds ratio?

Non-collapsibility means the crude (marginal) OR can differ from the weighted average of stratum-specific ORs even when there is no confounding. This is a mathematical property of the OR (unlike the risk ratio or risk difference), and the change-in-estimate approach should account for this limitation.

Question 13: An instrumental variable (IV) must satisfy which key condition?

An instrumental variable must satisfy the exclusion restriction: it affects the outcome only through its effect on the exposure, with no direct path to the outcome and no shared causes with the outcome. This allows estimation of causal effects even with unmeasured confounders.

Question 14: Sensitivity analysis for unmeasured confounding helps researchers by:

Sensitivity analysis does not identify specific confounders or prove their absence. Instead, it systematically explores how strong a hypothetical unmeasured confounder would need to be (in terms of prevalence and association with disease) to explain away the observed result — helping assess the robustness of findings.

Question 15: Which statement about confounders at the population level versus the study sample level is correct?

A variable that is a confounder in the source population may not confound in a specific study sample if, by chance or design, it is equally distributed across exposure groups. Confounding depends on the actual association between the variable and exposure in the study data.
✦ Complete the final reflection above before submitting

Congratulations!

You have successfully completed Lesson 12: Confounding and Causal Inference.

You now understand the principles of confounding, methods for its detection and control, and how to evaluate the robustness of findings in observational research.

This is the closing lesson of HSCI 341. Across 12 lessons you've assembled a complete causal-inference toolkit — surveillance, sampling, questionnaire design, frequency, screening, association, study design, hybrid and controlled designs, validity, and confounding control. Next stop: HSCI 410 — Exploratory Data Analysis for Epidemiology (12 lessons), where you'll put these methods to work in R with regression-based adjustment, model diagnostics, and applied data analysis. The methods you've been building since Lesson 1 finally come together as a working public-health skill set, ready to be operationalised in code.