Advanced epidemiology: bias, confounding and effect modification

In short

Bias, confounding and effect modification are the three reasons an observed exposure-outcome association may not be the causal effect you think it is - bias from flawed selection or measurement, confounding from a common cause, and effect modification from the effect genuinely differing across subgroups. Distinguishing them decides whether a study's finding is a measurement artefact (to be prevented in design), a mixing of effects (to be adjusted), or a real biological or social phenomenon (to be reported separately by subgroup). It is the core of MPH advanced epidemiology papers at AIIMS, PGIMER, SCTIMST, TISS and the state public health universities, and of ICMR/NIE, IIPS and NFHS-type analytical work. Interviews at ICMR institutes, NGO research units, CROs (Syneos, IQVIA, Parexel), pharmacovigilance teams and health-insurance analytics test it through "how would you handle confounding here" scenarios. Mastery is judged by whether you can draw the DAG, choose the adjustment set, and compute a stratified and Mantel-Haenszel estimate by hand.

Explained

Validity, error and the three threats

• Internal validity - the estimate is correct for the study population studied; external validity (generalisability) - it transfers to a target population. Bias destroys internal validity first.
• Random error (chance) shrinks with sample size and is quantified by confidence intervals; systematic error (bias) does not shrink with n - a bigger biased study is a more precisely wrong study.
• Three distinct problems: bias (a flaw in how subjects were selected or data measured), confounding (a real but non-causal path through a common cause), effect modification (the effect truly varies across strata).
• Bias is prevented at design stage (sampling, blinding, validated instruments); confounding can be handled at design *or* analysis; effect modification is never "corrected" - it is described.
• Direction: bias towards the null (dilution) or away from the null (exaggeration); a qualitative bias reverses the direction of the association.

Selection bias - types and Indian examples

• Definition: the association between exposure and outcome differs between those selected into the study and those eligible, because selection (or retention) depends on both exposure and outcome.
• Berkson's (admission rate) bias - hospital controls are admitted for reasons correlated with exposure; a hospital-based case-control study of smoking in a tertiary centre like AIIMS over-represents smokers among controls, biasing OR towards null.
• Prevalent (incidence-prevalence or Neyman) bias - studying survivors only; prevalent cases of MI in a clinic miss rapid deaths, so exposures that worsen survival look protective.
• Healthy worker effect - occupational cohorts (coal, ship-breaking at Alang, textile mills) are healthier than the general population; comparing them with general-population mortality understates occupational risk. Use an internal comparison group (low-exposed workers).
• Loss to follow-up / attrition bias - differential drop-out by exposure and outcome; in a TB treatment cohort, loss of patients who moved for work biases cure rates upward.
• Non-response and volunteer (self-selection) bias - responders to a health survey differ systematically; volunteers in screening camps are health-conscious.
• Immortal time bias - person-time before a patient could possibly have been exposed is misassigned to the exposed group, making treatment look protective; classic in prescription-database studies.
• Collider bias / selection on a collider - conditioning on a variable caused by both exposure and outcome induces an association; the obesity-paradox and the "birth-weight paradox" are standard instances.
• Prevention: population-based sampling, multiple control groups, high response rate, defined cohort entry (new-user design), sensitivity analysis for drop-outs.

Information (measurement) bias and misclassification

• Definition: error in measuring exposure, outcome or covariates. Classified by what is misclassified and by whether the error depends on the other variable.
• Non-differential misclassification - error rate equal across comparison groups. For a binary exposure with two levels it usually biases towards the null; with three or more exposure levels it can bias either way.
• Differential misclassification - error depends on the outcome (or exposure); direction unpredictable. Sub-types:
  • Recall bias - cases remember exposures better; mothers of malformed infants recall drug use in pregnancy more fully than control mothers.
  • Interviewer / observer bias - knowledge of case status influences probing; prevent with blinding and structured schedules.
  • Reporting / social-desirability bias - under-reporting of alcohol, tobacco and sexual behaviour in NFHS-type surveys; biosocial validation (cotinine, breath CO) helps.
  • Diagnostic suspicion bias - exposed subjects are investigated more intensively, so more outcomes are found (surveillance/detection bias).
• Ecological fallacy - inferring individual-level association from group-level data (district literacy vs district IMR).
• Regression dilution / attenuation - random error in a continuous exposure (one-off BP or dietary recall) attenuates the slope towards the null; corrected by validation sub-studies and regression calibration.
• Quantifying it: sensitivity and specificity of the measurement, kappa for agreement, and quantitative bias analysis (probabilistic sensitivity analysis) to reconstruct the corrected estimate.
• Prevention: validated and translated instruments (back-translation for Indian languages), blinding, objective records (ANC cards, Ni-kshay/TB records), standardised training, duplicate measurements, memory aids and calendars.

Confounding - criteria, assessment and control

• A confounder must satisfy three conditions: (1) associated with the exposure; (2) an independent risk factor for the outcome in the unexposed; (3) not an intermediate on the causal pathway from exposure to outcome.
• Common-cause structure: C → E and C → D creates a backdoor path E ← C → D that transmits a non-causal association. Blocking it (adjustment) removes the confounding.
• Do NOT adjust for: a mediator (over-adjustment - removes the very effect you are measuring), a collider (induces bias), or a variable affected by the exposure. Adjusting for a pure risk factor for the outcome only changes precision, but adjusting for an instrument (a variable affecting the outcome only through the exposure) *amplifies* any residual unmeasured confounding - "Z-bias" / bias amplification.
• Detection: compare crude and adjusted measures. A difference of roughly 10% or more in the (log) effect measure is the conventional signal of confounding - a judgement rule, not a test. Do not use a significance test on the confounder to decide.
• Design-stage control: randomisation (handles unmeasured confounders too), restriction (narrow eligibility), matching (individual or frequency - in case-control studies matching must be followed by a matched analysis), specification of a homogeneous cohort.
• Analysis-stage control: stratification, Mantel-Haenszel pooled estimates, standardisation (direct and indirect), multivariable regression (logistic, Poisson, Cox), propensity scores (matching, weighting, stratification), inverse probability weighting, instrumental variables, difference-in-differences, fixed-effects designs (self-controlled case series, case-crossover).
• Residual confounding - remains after adjustment because the confounder was measured crudely, misclassified, or unmeasured; a persistent criticism of nutritional and socioeconomic epidemiology in India, where caste, SLI/wealth quintile and education are proxies for much else.
• Negative confounding - the confounder masks a true effect, so the adjusted estimate is further from the null than the crude.
• Simpson's paradox - the direction of the association reverses on stratification; an extreme form of confounding.
• Quantifying unmeasured confounding: the E-value - the minimum risk ratio an unmeasured confounder would need with both exposure and outcome to explain away the observed association.

Effect modification and interaction

• Effect modification - the magnitude (or direction) of the exposure's effect differs across levels of a third variable M; evaluated by comparing stratum-specific estimates, not by any single pooled estimate.
• Interaction is the statistical term (product term in a model); effect modification is the epidemiological concept. In a causal framework they are not identical: effect modification is about a variable that stratifies the population, interaction about two interventions.
• Scale dependence is the central exam point: interaction on the multiplicative scale (RR) and on the additive scale (risk difference) are different questions. Two exposures with equal, non-null RRs and different baseline risks always interact additively even with no multiplicative interaction. Additive scale is the one that matters for public health (how many cases prevented).
• Measures of additive interaction in case-control data (Rothman): RERI (relative excess risk due to interaction), AP (attributable proportion due to interaction), S (synergy index).
• Qualitative (crossover) effect modification - the effect is protective in one stratum and harmful in another; much rarer and demands scrutiny.
• Testing: test of homogeneity across strata - Breslow-Day test or the Mantel-Haenszel/Woolf chi-square for heterogeneity, or a likelihood-ratio test on the product term. These tests are underpowered; absence of a significant interaction is not evidence of homogeneity.
• Practical rule: if strata are heterogeneous, report stratum-specific estimates and do not pool; if homogeneous, report the pooled (M-H or adjusted) estimate.
• Examples: smoking and asbestos (synergistic for lung cancer); HbS heterozygosity modifying malaria risk; thinness modifying the effect of gestational diabetes; age modifying the effect of air pollution on respiratory admissions in Delhi.

Directed acyclic graphs and the structural view

• A DAG is a graph of nodes (variables) and single-headed arrows (direct causal effects) with no cycles; it encodes assumptions explicitly.
• Path types: causal (directed) path E → M → D; backdoor path through a common cause; a collider is a node with two arrows into it (E → K ← D).
• Blocking rules (d-separation): a path through a non-collider is blocked by conditioning on it; a path through a collider is open when you condition on the collider (or its descendant) and closed otherwise.
• Backdoor criterion - a set Z is sufficient for adjustment if it blocks every backdoor path from E to D and contains no descendant of E. This is how an adjustment set is chosen, not by "adjust for everything measured".
• M-bias - adjusting for a pre-exposure variable that is a collider between two unmeasured causes creates bias; a counter-example to "always adjust for pre-exposure covariates".
• Table 2 fallacy - interpreting every coefficient in one multivariable model as a causal effect; only the exposure's coefficient has the intended interpretation under that adjustment set.
• Tools: DAGitty (free, browser-based) for deriving minimal sufficient adjustment sets; STROBE reporting guidance expects confounders and their handling to be stated.

Indian context, ethics and reporting

• Reporting: STROBE for observational studies, CONSORT for trials, RECORD for routine-data studies; Indian journals (IJMR, IJPH, IJCM) require these.
• Ethics and governance: ICMR National Ethical Guidelines for Biomedical and Health Research Involving Human Participants, 2017; New Drugs and Clinical Trials Rules, 2019 (CDSCO) for trials; registration on CTRI (Clinical Trials Registry - India, ICMR-NIMS) is required before enrolment for trials.
• Data protection: the Digital Personal Data Protection Act, 2023 is enacted and the DPDP Rules, 2025 are notified, but the Data Fiduciary duties (notice, consent, breach intimation, erasure) apply only from 13 May 2027; until then IT Act section 43A and the SPDI Rules, 2011 govern sensitive health data. Research use also follows ICMR guidance on anonymisation.
• Indian data sources where these issues bite: NFHS-5 (2019-21) and NFHS-6 (fieldwork concluded; report release staggered - check the IIPS release), SRS, HMIS, Ni-kshay (TB), CGHS/PM-JAY claims, ICMR-INDIAB; survey weights and cluster design must be used or estimates are biased.
• Health-insurance and claims analytics (PM-JAY, private insurers) suffer severe selection and immortal-time bias; new-user active-comparator designs are the standard remedy.

Key points

• Internal validity - correctness of the estimate for the studied population; bias is the threat to it.
• Systematic error - does not reduce with sample size, unlike random error.
• Selection bias - selection depends jointly on exposure and outcome; prevented in design, not fixed by adjustment.
• Berkson's bias - hospital controls' admission linked to exposure, distorting the odds ratio.
• Healthy worker effect - occupational cohorts are healthier than the general population; use internal comparisons.
• Immortal time bias - unexposed person-time wrongly credited to the treated group, inflating apparent benefit.
• Recall bias - differential recall by case status; a case-control-specific information bias.
• Non-differential misclassification - usually biases a binary exposure's effect towards the null.
• Confounder - associated with exposure, independent risk factor for outcome, not an intermediate.
• Backdoor path - non-causal path E ← C → D; adjustment must block it.
• Collider - common effect of two variables; conditioning on it *creates* bias.
• Mediator - on the causal path; adjusting for it is over-adjustment.
• 10% rule - a 10% or greater change between crude and adjusted estimates signals confounding.
• Mantel-Haenszel estimate - weighted pooled OR/RR across strata, valid only if strata are homogeneous.
• Simpson's paradox - stratification reverses the direction of the crude association.
• Effect modification - stratum-specific effects genuinely differ; reported, never adjusted away.
• Scale dependence - additive and multiplicative interaction answer different questions; additive drives public-health impact.
• Breslow-Day test - test of homogeneity of odds ratios across strata; low power.
• E-value - minimum confounder strength needed to explain away an association.

Formulas and examples

Example 1 - Confounding by age, with Mantel-Haenszel adjustment. A case-control study in a Pune hospital examines tobacco chewing and oral cancer.

Crude table: exposed cases a = 300, exposed controls b = 200, unexposed cases c = 100, unexposed controls d = 400.

• Crude OR = (300 × 400)/(200 × 100) = 120000/20000 = 6.0.

Stratified by age:

• OR_MH numerator = (60×360)/600 + (240×40)/400 = 36 + 24 = 60.
• OR_MH denominator = (140×40)/600 + (60×60)/400 = 9.333 + 9.0 = 18.333.
• OR_MH = 60/18.333 = 3.27.
• Change from crude: on the log scale, (ln 6.0 − ln 3.27)/ln 3.27 = (1.792 − 1.185)/1.185 = 51% - far above 10%, so age confounds strongly. Stratum ORs 3.86 and 2.67 are reasonably close, so pooling is defensible; a Breslow-Day test would formally check this.

Example 2 - Effect modification, and why the scale matters. A cohort of 2,000 workers studies silica dust and tuberculosis, stratified by HIV status.

• RR is 2.0 in both strata - no multiplicative effect modification.
• RD is 25 per 1,000 against 60 per 1,000 - strong additive effect modification: the same relative effect produces 2.4 times the excess cases among HIV-positive workers.
• Public-health reading: dust control in the HIV-positive group prevents 60 cases per 1,000 exposed against 25 per 1,000 - so target it there first. Reporting "no interaction" from the RR alone would hide this.

Example 3 - Simpson's paradox (qualitative confounding). Two hospitals' surgical mortality:

• Crude: Hospital A looks more than twice as deadly (8.0% vs 3.6%).
• Within each case-mix stratum, A is better (2.0 < 2.5 and 10.0 < 12.0). Case mix (a confounder: A takes 75% high-risk patients, B only 11%) reversed the direction.
• Direct standardisation to a standard population of 1,000 low-risk and 1,000 high-risk: A = (0.020 + 0.100)/2 = 6.0%; B = (0.025 + 0.120)/2 = 7.25% - the correct comparison.

Example 4 - Non-differential misclassification biases towards the null. True cohort: exposed 1,000 with 200 cases (risk 0.20); unexposed 1,000 with 100 cases (risk 0.10); true RR = 2.0. The exposure questionnaire has sensitivity 0.80 and specificity 0.80.

• Classified-exposed group = 0.80 of true exposed + 0.20 of true unexposed = 800 + 200 = 1,000 people; cases = 0.80×200 + 0.20×100 = 160 + 20 = 180 → risk 0.180.
• Classified-unexposed group = 200 + 800 = 1,000 people; cases = 40 + 80 = 120 → risk 0.120.
• Observed RR = 0.180/0.120 = 1.50 against a true 2.0 - the measurement error alone destroyed half the excess risk. No sample size fixes this.

Example 5 - RERI and the E-value. For joint exposure to smoking and silica dust: RR₁₀ (smoking only) = 3.0, RR₀₁ (dust only) = 2.0, RR₁₁ (both) = 8.0.

• RERI = 8.0 − 3.0 − 2.0 + 1 = 4.0 → considerable additive interaction (synergy).
• AP = 4.0/8.0 = 0.50 - half the risk in the doubly exposed is attributable to interaction.
• S = (8 − 1)/[(3 − 1) + (2 − 1)] = 7/3 = 2.33 → synergy.
• Multiplicative check: 3.0 × 2.0 = 6.0 against observed 8.0, ratio 8/6 = 1.33 - positive but modest on this scale; the scales disagree in emphasis, which is the point.
• For an observed RR = 2.0, E-value = 2.0 + √(2.0 × 1.0) = 2 + 1.414 = 3.41: an unmeasured confounder would need RR ≈ 3.4 with both exposure and outcome to explain it away - implausible for most measured covariates, which strengthens the causal claim.

Where it is used

• ICMR institutes and NIE Chennai, NCDC, state IDSP/IHIP units - outbreak case-control studies where confounding by age, sex and water source decides the implicated vehicle.
• Clinical research and CROs (IQVIA, Syneos, Parexel, Veeda, Lambda) - protocol and SAP writing: adjustment sets, pre-specified subgroups and interaction tests; CTRI registration and ICMR 2017 ethics compliance.
• Pharmacovigilance and real-world evidence teams - claims and EMR studies using new-user active-comparator designs, propensity scores and immortal-time-bias checks.
• National surveys and health policy (IIPS/NFHS, NSSO health rounds, NITI Aayog health index) - survey weights, cluster design, confounding by wealth quintile and education.
• Health-insurance and hospital analytics (PM-JAY, private insurers) - risk-adjusted mortality and readmission league tables, which are meaningless without case-mix standardisation.
• Roles - epidemiologist, biostatistician, research officer (ICMR/NHM), medical writer, RWE analyst, monitoring-and-evaluation specialist in NGOs (PHFI, Jhpiego, PATH, Karuna Trust).

Interview questions

• Q: How do you distinguish confounding from effect modification? A: Confounding is a nuisance mixing of effects, shown by a crude estimate differing from the adjusted one; effect modification is a real difference in the effect across strata, shown by heterogeneous stratum-specific estimates. One is adjusted away, the other is reported.
• Q: What three criteria must a confounder meet? A: It must be associated with the exposure, be an independent risk factor for the outcome among the unexposed, and not lie on the causal pathway between exposure and outcome.
• Q: Why is adjusting for a mediator wrong? A: The mediator carries part of the exposure's causal effect, so conditioning on it removes exactly what you are trying to estimate - over-adjustment bias.
• Q: What is collider bias and give an example? A: Conditioning on a common effect of exposure and outcome induces a spurious association; conditioning on hospitalisation, which both a disease and a risk factor cause, is the classic case and underlies the obesity paradox.
• Q: Which way does non-differential misclassification bias a binary exposure? A: Towards the null, provided misclassification is independent of outcome and the exposure has only two levels; with more than two levels the direction is not guaranteed.
• Q: What is immortal time bias and how do you avoid it? A: Person-time during which the outcome could not have occurred is assigned to the treated group, exaggerating benefit; avoid it with a new-user design and a time-zero defined identically for both groups.
• Q: When is a Mantel-Haenszel pooled estimate inappropriate? A: When the stratum-specific estimates are heterogeneous - that is effect modification, and pooling hides it; report stratum-specific estimates instead.
• Q: Can randomisation remove confounding completely? A: It removes systematic confounding in expectation, including by unmeasured factors, but chance imbalance remains in any single trial - which is why baseline tables and pre-specified adjustment are still used.
• Q: Why does interaction depend on the scale? A: Additive and multiplicative models ask different questions; two exposures with the same risk ratio but different baseline risks generate different excess risks, so additive interaction can exist with no multiplicative interaction.
• Q: What does an E-value of 1.5 tell you? A: An unmeasured confounder associated with both exposure and outcome by a risk ratio of only about 1.5 could explain away the observed association - weak evidence of causation.
• Q: How is the healthy worker effect handled? A: Compare exposed workers with less-exposed workers from the same workforce rather than with the general population, and allow for a lag in exposure-response analysis.
• Q: Crude OR 4.0, adjusted OR 4.1 - what do you conclude? A: Change is about 2% on the log scale, well below 10%, so that variable is not a meaningful confounder here; it may still be a precision variable or an effect modifier, which heterogeneity testing would show.

Common mistakes

• Calling a variable a confounder because the confounder-outcome association is statistically significant, instead of applying the three criteria and the crude-versus-adjusted comparison.
• Adjusting for everything measured - sweeping in mediators and colliders and creating bias rather than removing it.
• Reporting a pooled Mantel-Haenszel estimate when the stratum-specific estimates clearly differ, which buries effect modification.
• Testing for interaction on the ratio scale only, concluding "no interaction", and missing a large additive difference in prevented cases.
• Assuming misclassification always biases towards the null - true only for non-differential error on a binary exposure.
• Treating selection bias as something adjustment can fix; once the sample is selected on exposure and outcome, only design changes or quantitative bias analysis help.
• Matching in a case-control study and then analysing it unmatched, or matching on the exposure itself and destroying the association.
• Interpreting every coefficient of one multivariable model as a causal effect - the Table 2 fallacy.

Related topics

Epidemiology: principles, measures and study designs · Causal inference basics · Multiple regression · Biostatistics for health sciences · Systematic reviews and meta-analysis · Statistical computing with R