2  Epidemiologic Measures and Study Design

2.1 Learning objectives

By the end of this chapter you should be able to:

  • Compute and interpret the standard epidemiologic measures: prevalence, incidence rate, cumulative incidence, risk ratio, odds ratio, rate ratio.
  • Choose between cohort, case-control, and cross-sectional designs for a given research question, and articulate the tradeoffs.
  • Distinguish confounding, effect modification, selection bias, and information bias, and recognise each in applied work.
  • Apply the modern target-trial-emulation framework to a proposed observational analysis.

2.2 Orientation

Chapter 1 established estimands and study designs at the framework level. This chapter operationalises them: how to compute the standard measures, how to choose designs, how to recognise the biases that threaten each design’s validity. The material is the entry point to applied epidemiology and the conceptual scaffolding for the causal-inference chapters that follow.

The chapter is organised around three threads. Measures: prevalence, incidence, and the rate / risk / odds ratios that summarise associations and effects. Designs: cohort, case-control, cross-sectional, with explicit attention to when each is the right choice. Biases: confounding, selection, information, with examples drawn from public-health practice.

Modern epidemiology has converged on target-trial emulation (Hernán & Robins, 2016) as the discipline for observational causal inference. The target-trial framework asks the analyst to specify the hypothetical randomised trial that would answer the question, and then to design the observational analysis to emulate that trial as closely as possible. The chapter ends by walking through this framework on a concrete example.

2.3 The statistician’s contribution

Three judgements at the centre of epidemiologic design are not delegable.

(Judgement 1.) Choose the measure that matches the decision. A risk ratio of 1.5 sounds different from a risk difference of 0.05, but they may describe the same data. The right measure is the one that informs the decision under consideration: relative measures for mechanism and aetiology questions; absolute measures (risk differences, NNT) for clinical and policy decisions where the baseline risk matters. The biostatistician chooses the measure deliberately and presents the alternative when the decision benefits.

(Judgement 2.) The design constrains the inference. A case-control study cannot estimate prevalence; a cross-sectional study cannot establish temporal order; an unmatched cohort is vulnerable to confounding by indication. The biostatistician identifies what the chosen design can and cannot say, and limits the report’s claims accordingly. Reviewers will identify the limit if the analyst does not; better to disclose than to defend.

(Judgement 3.) Bias is not a hypothesis test. The question is not ‘is there confounding’ (the answer is almost always yes) but ‘how large is the bias relative to the effect, and in which direction’. The biostatistician quantifies bias through sensitivity analyses (E-values, tipping-point analyses, negative controls) rather than asserting its absence. The discipline applies as much to RCTs (where confounding is in expectation zero but in any specific trial may be present) as to observational studies.

These judgements distinguish epidemiologic work that informs decisions from work that produces numbers in search of a question.

2.4 Prevalence and incidence

Prevalence is the proportion of a population with the condition at a point in time: \[ P = \frac{\text{cases at time } t}{\text{population at time } t} \] Prevalence is dimensionless. It depends on incidence (how often the condition is acquired) and duration (how long it lasts). High-prevalence conditions can have either high incidence or long duration or both.

Incidence rate is the number of new cases per person-time: \[ \text{IR} = \frac{\text{new cases in period}}{\text{person-time at risk}} \] Person-time has units (person-years, person-months). Incidence rate has the corresponding inverse units (per person-year). It is the rate parameter of the underlying point process.

Cumulative incidence is the proportion of an initially-disease-free cohort that develops the condition over a defined period: \[ \text{CI}(t) = \Pr(T \le t) \] Cumulative incidence is dimensionless. For short follow-up with a constant rate, \(\text{CI}(t) \approx \text{IR} \cdot t\); the approximation breaks at longer follow-up. The full relationship via the survival function (Ch 7) is \(\text{CI}(t) = 1 - S(t)\).

The three measures answer different questions: prevalence tells you the burden at a moment; incidence rate tells you how fast new cases appear; cumulative incidence tells you the total proportion affected over a follow-up period. Reports often confuse these; distinguish them carefully.

2.5 Risk, rate, and odds ratios

Three ratios summarise associations between an exposure and an outcome.

Risk ratio (RR): ratio of cumulative incidence between exposed and unexposed. \[ \text{RR} = \frac{\text{CI}_{\text{exposed}}}{\text{CI}_{\text{unexposed}}} \]

Rate ratio (or hazard ratio in survival contexts): ratio of incidence rates. \[ \text{IRR} = \frac{\text{IR}_{\text{exposed}}}{\text{IR}_{\text{unexposed}}} \]

Odds ratio (OR): ratio of odds of disease. \[ \text{OR} = \frac{p_{\text{exposed}}/(1-p_{\text{exposed}})}{p_{\text{unexposed}}/(1-p_{\text{unexposed}})} \]

When the outcome is rare (\(p \ll 0.1\)), OR \(\approx\) RR. For common outcomes, OR exaggerates effect size relative to RR; reporting only OR for a common outcome can mislead.

The choice between measures depends on the design and the question:

  • RCT or cohort, common outcome: prefer RR or risk difference. Logistic regression’s OR is a software default but not always the right reporting choice.
  • Case-control: OR is what the design naturally estimates; under the rare-disease assumption it approximates the RR.
  • Cohort with time-to-event: rate ratio or hazard ratio (Ch 7).

Question. A cohort study estimates an OR of 2.5 for the association between a binary exposure and a binary outcome. The unexposed risk is 0.30. What is the RR?

Answer.

The unexposed odds is 0.30/0.70 = 0.43; the exposed odds is 2.5 × 0.43 = 1.07; the exposed risk is 1.07/(1+1.07) = 0.52. The RR is 0.52/0.30 = 1.73, much smaller than the OR of 2.5. For a common outcome, reporting the OR makes the effect look larger than it is. The RR is the more interpretable measure here.

2.6 Cohort studies

Subjects are sampled by exposure (or unselectively) and followed forward in time; outcomes are recorded as they occur. Strengths:

  • Establishes temporal order (exposure precedes outcome).
  • Estimates absolute risks and rates directly.
  • Suitable for causal inference under a no-unmeasured-confounding argument plus appropriate adjustment.

Weaknesses:

  • Expensive and slow; long follow-up to accrue events for rare outcomes.
  • Loss to follow-up creates differential bias if loss correlates with exposure or outcome.
  • Confounding by indication when exposure is treatment-like.

Cohorts can be prospective (assembled at exposure, followed forward) or retrospective (assembled from records that already exist, with exposure and outcome already observed). Retrospective cohorts use the prospective machinery on records data; the analyst must take care that exposure was recorded before outcome and not produced by knowledge of the outcome.

2.7 Case-control studies

Subjects are sampled by outcome status: cases (with the disease) and controls (without). Exposure is then assessed retrospectively. Strengths:

  • Efficient for rare outcomes (cases are oversampled relative to their population frequency).
  • Multiple exposures can be studied for the same outcome.
  • Often the only feasible design for slow-developing conditions.

Weaknesses:

  • Recall bias when exposure is self-reported (cases may remember exposure differently from controls).
  • Selection bias is a constant threat: how were the controls chosen?
  • Estimates only the OR; no absolute risks.

The OR from a case-control study approximates the RR in the underlying population only when the outcome is rare. For common outcomes, the OR is the parameter the design naturally estimates and should be reported as such.

Nested case-control designs sample cases and a matched set of controls from within an existing cohort, combining the efficiency of case-control with the defensibility of cohort sampling.

2.8 Cross-sectional studies

A snapshot of a population at one time point. Estimates prevalence and prevalence ratios. Cannot establish temporal order: if exposure and outcome are both observed at one time, you cannot tell which preceded.

Useful for surveillance and prevalence estimation; less useful for inference about causes (the temporal-order problem is fundamental, not addressable by adjustment). Many published cross-sectional studies overstate causal claims; the careful reader treats their associations as hypothesis-generating, not hypothesis-testing.

2.9 Confounding, effect modification, selection, information

Four threats to validity. Each requires a different response.

Confounding is a third variable that affects both exposure and outcome and biases the exposure-outcome association. The classic test: smoking confounds the coffee-lung-cancer association because smokers drink more coffee and smokers get lung cancer at higher rates. Adjustment, restriction, matching, or design (randomisation) addresses confounding. The identification assumption is no unmeasured confounding given the adjustment set; sensitivity analysis quantifies what unmeasured confounding would need to do to overturn the conclusion.

Effect modification (interaction) is when the effect of the exposure differs across levels of a third variable. Sex modifies the effect of cardiovascular medications; age modifies the effect of vaccinations. Effect modification is a feature of the data, not a bias; it is reported by stratification or interaction terms in the model.

Selection bias arises when inclusion in the study depends on both exposure and outcome. The classic example: hospital-based controls in a case-control study, where hospitalisation is itself associated with the exposure. Selection bias cannot be fixed by adjustment; it is addressed by design (sampling controls appropriately) or by sensitivity analysis (quantifying the magnitude of bias under plausible selection mechanisms).

Information (measurement) bias arises when exposure or outcome is mismeasured, and the mismeasurement correlates with the other variable. Differential misclassification is the worst case: cases recall exposure better than controls. Non-differential misclassification (random measurement error) generally biases toward the null. Validation studies and quantitative-bias analyses address information bias.

The four are distinct. A common error is to treat ‘confounding’ as a catch-all for ‘something is wrong with this association’; precision in naming the bias informs the right response.

2.10 Target-trial emulation

The discipline that has emerged for observational causal inference (Hernán & Robins, 2016, 2020):

  1. Specify the target trial. What randomised trial would answer the question if it could be run? Specify eligibility, treatment strategies, assignment, follow-up, outcome, intercurrent events.
  2. Identify the observational data that emulates the trial. Eligibility maps to inclusion at time zero; treatment strategies map to observed exposure patterns; assignment maps to the analyst’s adjustment for confounding.
  3. Document the emulation. Where the observational data fails to emulate the target trial (e.g., immortal-time bias from how exposure is defined in the records), name the failure and address it (typically by redefining time zero so exposure and eligibility are simultaneous).

The framework eliminates a class of common observational-design errors: immortal-time bias, prevalent-user bias, selection-on-treatment-after- baseline. Most published observational studies of drug effects can be substantially improved by applying the target-trial framework retroactively. The discipline has become standard practice in modern pharmacoepidemiology.

2.11 Worked example: target-trial emulation for SGLT2 inhibitors

The example from Chapter 1 (SGLT2 effectiveness in HFrEF, EHR data from three hospitals) is a textbook target-trial application.

Step 1. Specify the target trial. A hypothetical RCT enrols adult HFrEF patients within 30 days of diagnosis, randomises to SGLT2 vs. no SGLT2 (treatment policy: any subsequent treatment changes are followed under the assigned arm), follows for 12 months, and records all-cause mortality.

Step 2. Emulate. From the EHR cohort:

  • Eligibility. Adults aged 18+, HFrEF (EF < 40%) diagnosed during the study period. Exclude prior SGLT2 users (who would not be eligible for the hypothetical trial).
  • Time zero. Date of HFrEF diagnosis.
  • Treatment groups. ‘SGLT2 initiator’ = SGLT2 prescription within 30 days of time zero. ‘Non-initiator’ = no SGLT2 prescription within 30 days. Note: this requires defining the groups at time zero, before observing the treatment decision; common in target-trial emulation, awkward without it.
  • Follow-up. From time zero to 12 months, death, or end of records.
  • Confounding. Adjust for baseline confounders at time zero (age, sex, EF, NT-proBNP, eGFR, comorbidities, baseline medications). Use IPW (Ch 4).
  • Sensitivity. E-value for unmeasured confounding (Ch 4).

Step 3. Identify failures of emulation.

  • Patients who initiate SGLT2 between days 30 and 90 are misclassified as non-initiators in the observational data but would be in the initiator arm under treatment policy in the target trial. The target-trial framework calls this ‘misclassification of grace period’; the fix is either to extend the grace period or to use a clone-censor-weight approach.
  • Time zero is hard to define for patients diagnosed at outside hospitals and transferred in. Address by either restricting to in-network diagnoses or using a sensitivity analysis.

The target-trial protocol is now the analysis plan. Six months later, a reviewer asking ‘why this 30-day window?’ is answered by ‘the target trial defined treatment groups at time zero with a 30-day grace period; the alternative would be a different target trial’.

2.12 Collaborating with an LLM on epidemiologic study design

Three patterns that work.

Prompt 1: ‘Write the target trial for this observational study.’ Provide the research question and the data source.

What to watch for. The LLM produces a competent draft of the seven target-trial components (eligibility, treatment, assignment, follow-up, outcome, intercurrent events, analysis). It tends to under-specify the treatment-strategy definition and the time-zero question. Push back: ‘how would you define time zero given that exposure is observed in records, not assigned at time zero?’

Verification. Read the LLM’s target trial against Hernán & Robins (2016); check that all seven components are specified concretely and that the immortal-time issue is addressed.

Prompt 2: ‘Identify the threats to validity in this analysis.’ Provide the analysis description.

What to watch for. The LLM lists the standard biases (confounding, selection, measurement) but tends to be generic. Push for specific confounders, specific selection mechanisms, specific measurement-error patterns informed by the data source.

Verification. The LLM’s threats are a starting list; your knowledge of the data source is what specialises them. Add threats the LLM missed; remove ones that do not apply.

Prompt 3: ‘Compute the relevant epidemiologic measures from this 2x2 table.’ Provide the cell counts.

What to watch for. The LLM gets the arithmetic right for risk ratio, odds ratio, etc. It sometimes confuses the OR-RR distinction for common outcomes. Verify the specific case the LLM is computing.

Verification. Recompute by hand; the formulas are elementary.

The meta-pattern: LLMs are useful for drafting target-trial protocols and for listing the threats to validity in standard form. They cannot evaluate whether your specific data emulates the target trial well; that judgement is yours.

2.13 Principle in use

Three habits define defensible epidemiologic work.

  1. Match the measure to the decision. Relative measures for aetiology; absolute measures for policy and clinical decisions. Report both when the audience benefits.
  2. Apply the target-trial framework. Every observational causal analysis specifies its target trial and documents where the emulation succeeds or fails.
  3. Quantify bias rather than assert its absence. Sensitivity analyses (E-values, tipping points) are part of every causal analysis, not an afterthought.

2.14 Exercises

  1. For a published cohort study in your field, identify the prevalence, incidence rate, and cumulative incidence reported (or compute them from the reported data). Note the units of each.

  2. Take a 2x2 contingency table (exposed-vs-unexposed by outcome-vs-no-outcome) of your choice. Compute the risk ratio, the odds ratio, the rate ratio (assuming person-time is proportional to sample size), and the risk difference. Discuss when each measure is the right choice for reporting.

  3. Identify a published case-control study in your field. Identify how controls were sampled and whether the sampling could introduce selection bias. If yes, describe the likely direction.

  4. For an observational study of a drug effect, write the target-trial protocol following the seven components. Identify two specific places where the observational data will fail to emulate the target trial perfectly, and propose a remediation for each.

  5. Compute an E-value for an observed risk ratio of 1.6. What does the E-value tell you about the strength of unmeasured confounding required to explain away the association?

2.15 Further reading

  • Lash et al. (2021), Modern Epidemiology (4th edition). The reference textbook for the material in this chapter.
  • Hernán & Robins (2020), Causal Inference: What If. The open-access textbook that develops target-trial emulation in depth.
  • Hernán & Robins (2016), ‘Using big data to emulate a target trial when a randomized trial is not available’. The methods paper that defines the target-trial framework.
  • VanderWeele & Ding (2017), ‘Sensitivity analysis in observational research: introducing the E-value’. The reference for E-value sensitivity analysis.