Introduction and Overview

Earlier lessons of this course built the building blocks: causal logic, surveillance, sampling, questionnaire design, frequency, screening, and association. This lesson is a checkpoint that consolidates the observational study designs you first met in an earlier course (earlier lessons) and explicitly maps each design to the measures of association from an earlier lesson. The three content sections walk through this in order: cross-sectional studies (this section), cohort and case-control designs (a later section), and ecological studies plus an introduction to evidence synthesis via systematic reviews (a later section). Once the standard observational designs are consolidated, later lessons will introduce hybrid and controlled designs that combine or extend these basics.

Observational vs. Experimental Studies

All epidemiologic studies can be broadly classified into two categories based on whether the investigator assigns the exposure. In experimental studies (also called intervention studies or controlled trials), the researcher deliberately allocates exposure, for example assigning participants to receive a new treatment or a placebo. In observational studies, the researcher simply observes and measures exposures and outcomes as they occur naturally, without intervening.

This distinction matters enormously for causal inference. Experimental designs, particularly randomized controlled trials (RCTs), can establish exchangeability through random assignment. Exchangeability means the exposed and unexposed groups are alike in every other factor that affects the outcome, so a difference in outcomes can be credited to the exposure itself rather than to some background difference between the groups. This strengthens our ability to attribute differences in outcomes to the exposure (Concato, Shah, & Horwitz, 2000). Observational studies, by contrast, must contend with the possibility that exposed and unexposed groups differ in ways that also affect the outcome; that is, they must account for confounding. Vandenbroucke (2008) argues that observational and experimental research serve distinct epistemic purposes, discovery and evaluation, rather than sitting on a single ladder of rigour.

Descriptive vs. Analytic Studies

Within observational epidemiology, a further distinction exists between descriptive and analytic study designs.

Cross-Sectional Studies

A cross-sectional study measures exposure and outcome status simultaneously in a defined population at a single point in time (or over a short period). It provides a "snapshot" of the population, allowing researchers to estimate the prevalence of disease and the prevalence of various exposures.

Key Characteristics

• Timing: Exposure and outcome are assessed at the same time, with no follow-up period.
• Measure of disease frequency: Prevalence (not incidence), because you are measuring how many people currently have the condition.
• Measure of association: The prevalence ratio or prevalence odds ratio. Because exposure and outcome are measured simultaneously, temporal sequence is often unclear.
• Sampling: Participants are typically sampled from a defined population regardless of exposure or disease status.

Strengths and Limitations

Introduction and Overview

An earlier section reviewed cross-sectional designs, useful for prevalence estimation but limited for causal inference. This section turns to the two analytic designs that can support causal claims: cohort studies (sampling on exposure, following forward to disease) and case-control studies (sampling on disease, looking backward at exposure). Both produce specific measures of association you computed by hand in an earlier lesson.

Cohort Studies

A cohort study begins by identifying a group of individuals (a cohort) who are free of the outcome of interest, classifying them by exposure status, and following them over time to observe whether the outcome develops. The direction of inquiry moves from exposure to outcome, the same temporal direction as causation itself.

Types of Cohort Studies

Direction of Inquiry

Measures of Association in Cohort Studies

Before the formulas, it helps to fix the notation. Nearly every measure in this lesson is read off a 2×2 table that cross-classifies each person by exposure (the rows) and by disease (the columns). The four counts are labelled a, b, c, and d:

So a is the number of exposed people who develop the disease, and a + b is everyone who was exposed. That makes a/(a+b) the proportion of the exposed who get the disease and c/(c+d) the same proportion among the unexposed. With that picture in mind: because cohort studies follow participants over time and observe new cases, they can directly estimate incidence, which allows the calculation of:

• Risk Ratio (Relative Risk): The ratio of cumulative incidence in the exposed group to cumulative incidence in the unexposed group. RR = (a/(a+b)) / (c/(c+d)).
• Rate Ratio: The ratio of incidence rates (person-time denominators) in exposed vs. unexposed groups.
• Risk Difference (Attributable Risk): The absolute difference in incidence between exposed and unexposed groups.

Case-Control Studies

A case-control study begins by identifying individuals who have the outcome of interest (cases) and a comparable group who do not (controls). The investigator then looks backward in time to compare the exposure histories of the two groups. The direction of inquiry moves from outcome to exposure.

Selecting Cases and Controls

The validity of a case-control study depends critically on appropriate selection of cases and controls (Wacholder, McLaughlin, Silverman, & Mandel, 1992):

Measures of Association in Case-Control Studies

Because case-control studies do not follow a defined cohort over time, they cannot directly calculate incidence. Therefore, the risk ratio cannot be computed directly. The deeper reason is that the investigator decides in advance how many cases and how many controls to enrol, so the fraction of the sample that is diseased is fixed by that design choice rather than by how common the disease actually is; a proportion like a/(a+b) therefore does not estimate a genuine risk. Instead, the primary measure of association is the odds ratio (OR):

Comparing Cohort and Case-Control Designs

Introduction and Overview

Earlier sections covered designs that operate at the individual level. This section makes one final move, up to the group level, with ecological studies, and then steps back to ask how evidence from many such studies can be synthesized. The ecological fallacy you met in an earlier course reappears here as a specific limitation; systematic reviews are the formal answer to “what does the evidence as a whole say?”

Ecological Studies

An ecological study (also called a group-level or aggregate study) uses groups, rather than individuals, as the unit of analysis. Instead of measuring exposure and outcome in each person, the investigator compares exposure levels and disease rates across defined populations, such as countries, regions, or time periods.

Types of Ecological Studies

Click each card to learn more:

Group-Level Variables

A distinctive feature of ecological studies is their reliance on group-level variables. These can be classified into three types:

The Ecologic Fallacy

The ecologic fallacy is the most important limitation of ecological studies. It occurs when an association observed at the group level is incorrectly assumed to hold at the individual level (Robinson, 1950/2009; Morgenstern, 1995). Just because countries with higher fat consumption have higher breast cancer rates does not mean that the individuals within those countries who eat more fat are the same individuals who develop breast cancer.

Canadian Data Infrastructure for Cohort, Case-Control, and Ecological Designs

Most epidemiological work in Canada does not involve enrolling a fresh cohort. Instead, researchers reuse data that have already been collected through health-system encounters, surveys, environmental monitoring, and registries. Three pieces of national infrastructure show up repeatedly:

Evidence Synthesis: Systematic Reviews

No single study, regardless of design, can definitively establish a causal relationship. Scientific knowledge accumulates through the synthesis of evidence across multiple studies, populations, and designs. Systematic reviews are the formal method for achieving this synthesis.

What Is a Systematic Review?

A systematic review uses a pre-specified, transparent, and reproducible protocol to identify, appraise, and synthesize all available evidence on a specific research question (Higgins et al., 2019). Unlike a narrative review (where the author selects studies subjectively), a systematic review:

• Defines a precise research question (often using the PICO framework: Population, Intervention/Exposure, Comparison, Outcome).
• Conducts comprehensive, systematic searches of multiple databases.
• Applies explicit inclusion and exclusion criteria.
• Critically appraises the quality and risk of bias of each included study.
• Synthesizes findings quantitatively (meta-analysis) or qualitatively.

Meta-Analysis

When studies are sufficiently similar, their results can be combined statistically in a meta-analysis to produce a pooled estimate of effect (DerSimonian & Laird, 1986). Meta-analysis increases statistical power, provides more precise estimates, and can explore heterogeneity across studies (e.g., do results differ by study design, population, or exposure definition?).

# 2x2 cells
a <- 194; b <- 1588
c <- 303; d <- 1314

choose_measure <- function(a, b, c, d, design) {
  switch(design,
    "cross-sectional" = c(PR = (a/(a+b)) / (c/(c+d))),
    "cohort"          = c(RR = (a/(a+b)) / (c/(c+d))),
    "case-control"    = c(OR = (a*d) / (b*c)),
    stop("design must be one of: cross-sectional, cohort, case-control"))
}

choose_measure(a, b, c, d, "cross-sectional")
choose_measure(a, b, c, d, "cohort")
choose_measure(a, b, c, d, "case-control")

# side-by-side
designs <- c("cross-sectional", "cohort", "case-control")
sapply(designs, function(d_) choose_measure(a, b, c, d, d_))

Introduction and Overview

An earlier lesson consolidated the four standard observational designs. This lesson introduces the variants that combine or extend them. Hybrid designs are the answer to specific limitations of the standard four, such as rare or expensive exposures, transient triggers (Suissa, 1995), and surveillance data without obvious controls. The three content sections move from time-based case-only designs (this section: case-crossover and self-controlled case-series), through case-only comparison designs (a later section), to case-cohort and two-stage sampling designs (a later section) that subsample from larger cohorts to make biomarker-heavy studies affordable.

What Are Hybrid Study Designs?

By now you are familiar with the classic observational designs: cohort, case-control, and cross-sectional studies. Hybrid designs are variants of these classic designs that have been developed to address particular methodological challenges such as expensive covariates, rare exposures, and transient triggers, or surveillance data where traditional control selection is problematic.

This lesson covers six hybrid designs plus one important sampling strategy. Four of the hybrid designs use only cases (no separate control group), while two use a control series. The two-stage sampling design, by contrast, is a strategy that can be layered onto any of the traditional designs to enhance efficiency.

The Six Hybrid Designs at a Glance

Click any card to see a brief description of the design and its key feature.

Case-Crossover Studies

The case-crossover study is the observational analogue of the experimental crossover design. Each case serves as its own control by contrasting exposure during a defined time window before the event with exposure during one or more comparison time windows.

Maclure (1991) introduced the design to answer the “why now” question, in contrast to the “why me” question answered by traditional case-control studies. By using the same person as both case and control, the design automatically controls for all time-invariant confounders, including ones the investigator never measured or even thought of. Maclure and Mittleman (2000) review a decade of applications.

When Is a Case-Crossover Design Appropriate?

Defining the Risk Period and Control Period

Two design choices drive the validity of a case-crossover study: the length of the risk period (sometimes called the case-risk window) and the strategy for selecting control periods (sometimes called referent periods).

The risk period is the time during which the exposure, if causal, would have produced the event. Choosing a risk period that is too long increases the chance of detecting spurious associations; too short, and real associations may be missed. For physical exertion and myocardial infarction the risk window might be a few hours; for mobile phone use and motor vehicle crashes it might be five minutes; for air pollution effects on respiratory hospitalisations it is typically one day.

Strategies for Selecting Control Periods

Analysis of Case-Crossover Data

Because each case is matched to one or more control periods within the same individual, the data are analysed as if from a matched case-control study. With one control period per case, the data fit a 2×2 table and McNemar's test applies. Intuitively, this comparison ignores occasions when exposure was the same in both windows and asks, among the occasions where it differed, whether exposure fell in the risk window more often than in the control window. With multiple control periods, conditional logistic regression is the standard approach, and the exponentiated coefficient represents the change in odds of the event associated with a one-unit short-term increase in exposure.

When daily exposure data are available for the entire observation period (the “shared exposure” setting common in air pollution studies), the data can equivalently be analysed as a Poisson time series. The two analytical frameworks are mathematically linked when time-stratified referents are used.

Self-Controlled Case-Series Studies

The self-controlled case-series design (often shortened to “case-series” in this literature, but distinct from the descriptive case-series of clinical reports) was developed by Farrington (1995) largely for vaccine safety research. It is a close cousin of the case-crossover design but generalises the comparison from discrete control periods to all of an individual's observation time outside the risk window. Whitaker, Farrington, Spiessens, & Musonda (2006) provide an accessible tutorial.

The Logic of the Design

For each individual who has experienced the outcome of interest, an observation period is defined, namely a calendar window during which exposure history and event occurrence are tracked. Within that observation period, one or more risk periods are designated based on the biology of the exposure (e.g., 6–35 days after vaccination for febrile conditions). All remaining time within the observation period constitutes the control period.

The analysis compares the rate of events during risk time with the rate during control time, after adjusting for the duration of each. As with the case-crossover design, this is a within-person comparison: every time-invariant characteristic of the case (genetics, sex, baseline health) is automatically controlled by design. Age and season can be adjusted for analytically because they vary across the observation period.

# install.packages(c("gnm", "SCCS"))
library(gnm)

# Long-format SCCS data: 4 cases, each with risk and control periods
sccs <- data.frame(
  case   = rep(1:4, each = 2),
  period = rep(c("risk", "control"), 4),
  events = c(1, 0,  1, 0,  2, 1,  0, 1),
  pt     = c(30, 335, 28, 337, 30, 335, 29, 336)
)

# Conditional Poisson on case (each case is its own intercept)
fit <- gnm(events ~ period,
           offset = log(pt),
           family = poisson,
           eliminate = factor(case),
           data = sccs)
exp(coef(fit))                    # incidence rate ratio (risk vs. control)
exp(confint.default(fit))

Key Assumptions

Analysis

The standard analytic tool is a conditional Poisson regression model, where the outcome is the count of events in each risk and control time interval and the logarithm of the duration of each interval is the offset. The parameter of interest is the relative incidence, that is, the rate during the risk period relative to the rate during the control period.

Introduction and Overview

An earlier section covered designs that use each case as their own control across time. This section turns to designs that compare different kinds of cases to one another, useful when traditional controls are unavailable, when subtypes of disease have different aetiologies, or when surveillance data only contain ill people. Each design in this section sacrifices something in exchange for not needing a healthy control group.

Case-Case Studies

The case-case design is a variant of the case-control design in which the comparison group consists of cases of a different disease subtype drawn from the same surveillance system. McCarthy and Giesecke (1999) proposed it as an efficient way to identify risk factors that distinguish closely related etiological subgroups using routine surveillance data.

For example, the cases might be people infected with Salmonella Typhimurium, while the “controls” might be people infected with Salmonella Heidelberg. Both groups have salmonellosis (both are cases), but the design seeks to identify exposures that distinguish one serotype from the other.

When Is the Case-Case Design Useful?

Strengths and Limitations

Analysis

Case-case data are analysed by the same techniques as risk-based case-control studies, typically logistic regression. The exponentiated coefficient is interpreted as the relative odds of exposure between the two case subtypes, not as a risk ratio.

Case-Case-Control Studies

The case-case-control design (Kaye, Harris, Samore, & Carmeli, 2005) was developed to overcome a specific limitation of traditional case-control studies in the context of antimicrobial resistance. The original example was vancomycin-resistant Enterococcus (VRE) versus vancomycin-susceptible Enterococcus (VSE).

The Problem the Design Solves

Suppose you want to identify risk factors for VRE infection. A traditional case-control approach would compare VRE cases with non-infected controls. But many of the exposures associated with VRE (prior antibiotic use, prolonged hospitalisation, ICU stay) are also strong risk factors for VSE, and indeed for any hospital-acquired infection. So a traditional design tells you what causes hospital infection in general, not what specifically drives the resistant phenotype.

An alternative is a case-case design comparing VRE with VSE. But Kaye and colleagues argue against this: VRE often emerges from external sources (transmission of an already-resistant strain) rather than from within-patient evolution of a susceptible strain. So contrasting VRE directly with VSE conflates “risk of acquiring a resistant strain” with “risk of selection pressure on a susceptible one.”

The Case-Case-Control Solution

The design uses two case series (resistant and susceptible) and one control series (people without infection from the same source population). Two separate logistic regression models are fitted, one comparing each case series with the controls. The risk factors are then sorted into three categories.

Interpreting the Three Variable Categories

Design Considerations

• First positive culture per patient. Only the first positive culture should be included to avoid double-counting; for nosocomial infection studies, restrict to cultures taken >48 hours after admission.
• Source population matters. Controls should come from the same source population as the cases. For nosocomial infections, controls should be other patients hospitalised >48 hours, ideally with documented negative cultures for both phenotypes.
• Confounding control. Because there is only a single control series, restricted sampling and matching are difficult. Confounding is typically handled through multivariable unconditional logistic regression.

Case-Only Studies

The case-only design uses only cases, with no observed control group recruited. The expected exposure distribution in the hypothetical “control population” is derived from theoretical or external sources. The design originated in genetic epidemiology, where the population frequency of common alleles can often be specified from external reference data (Khoury & Flanders, 1996).

What the Design Can and Cannot Estimate

The intuition is this: among cases, if a genetic risk factor and an environmental exposure are independent in the source population but appear together more often than expected by chance, that excess co-occurrence is evidence of statistical interaction on the multiplicative scale. If the gene and exposure were also causally associated in the source population (not independent), this signal would be confounded.

Required Assumptions

• Independence in the source population. The exposure and the proposed effect modifier (often a gene, but can be sex, age, or another stable trait) must be independent in the population from which cases arose. For a heritable polymorphism not influenced by the environmental exposure, this is biologically plausible.
• Stable, well-defined effect modifier. Genetic variants, sex, race, and age are common choices because they don't change over time and can be measured reliably.
• The disease must be rare. Like many odds-ratio-based estimators, the case-only interaction estimate approximates the true interaction parameter most closely when the outcome is rare in the source population.

Recent Extensions Beyond Genetics

The design has been extended to study how non-genetic stable characteristics modify the effects of time-varying exposures. Armstrong (2003) and Schwartz (2005) used case-only designs to ask whether sex, race, age, or socioeconomic class modify the effect of extreme weather on mortality. Because age, sex, and socioeconomic class can reasonably be considered independent of daily weather exposures, the case-only approach yields a valid interaction estimate.

Analytic Logic

Suppose we are interested in whether sex modifies the effect of an extreme heat day on mortality. A case-only logistic regression takes the form:

The logic feels strange at first because we appear to be modelling a covariate (sex) as a function of an exposure. But this is mathematically equivalent to a Poisson model of mortality count as a function of heat, sex, and a heat×sex interaction term, where the case-only regression coefficient is the interaction term. The trick is that we never need a control group at all; the “control” expectation is built into the assumed independence of sex and heat in the source population.

Introduction and Overview

Earlier sections were about case-only designs. This section returns to designs that use cohorts as their backbone but subsample from them to make expensive measurements feasible. Both case-cohort and two-stage designs let you mount essentially a cohort study while only paying for biomarker measurements on a fraction of the participants, the kind of design that makes large biobanks practical.

Case-Cohort Studies

The case-cohort design, introduced by Prentice (1986), combines features of cohort and case-control studies. From a defined source cohort, the investigator draws a random sample called the subcohort at the start of follow-up. Detailed exposure and covariate data are obtained on the subcohort. As follow-up proceeds, all incident cases that arise from the full source cohort, whether or not they happen to fall within the subcohort, are also studied.

The design has the same advantages as a full cohort study (clear temporal ordering, multiple outcomes, direct disease frequency estimates) but achieves them with much smaller measurement costs because expensive covariate or biomarker assays are performed only on the subcohort plus the cases, not on the entire source cohort.

The Big Win: Multiple Outcomes from a Single Subcohort

Risk-Based vs. Rate-Based Designs

Practical Considerations

• Eligibility for the subcohort. Members must be willing to provide health history, lifestyle data, and (often) biological samples. Stratified sampling can ensure that the subcohort's covariate profile matches anticipated cases (e.g., over-sampling young adults if young-adult disease is the focus).
• Stored specimens. Serially stored tissue or blood samples allow detection of exposure changes over time and support post-hoc biomarker assays as new hypotheses emerge.
• Sampling adjustments for non-response. If 20% are sampled but only 80% of those agree to participate, the weighting should reflect the actual participation, not the original sampling probability.
• Robust standard errors are recommended for case-cohort analyses to account for the sampling variability.
• Clustering of cases. If cases tend to be diagnosed at the same clinic, marginal models with adjusted variances or frailty models should be used to account for within-cluster correlation.

Two-Stage Sampling Designs

A two-stage (or two-phase) sampling design is a strategy that can be layered on top of any traditional design, whether cohort, case-control, or cross-sectional. The first stage collects readily available, inexpensive data on a large group. The second stage collects more detailed (and usually more expensive) data on a strategically selected subsample.

Why Two-Stage Designs Make Sense

Three Common Use Cases

How to Sample at Stage 2

The key design question in any two-stage study is: how should we choose whom to include in the expensive second stage? The optimal answer depends on the design.

A Worked Two-Stage Case-Control Sampling Strategy

Suppose your stage 1 data come from a hospital registry of 50,000 pregnancies. From the registry you can identify 2,000 birth-defect cases and 48,000 non-cases. A crude (and possibly mismeasured) exposure indicator, namely whether the mother held a job classified as “industrial”, is available for everyone.

Stage 1 cross-classification might look like this:

For stage 2, balanced sampling across the four cells is the most efficient strategy. Suppose your budget allows 400 detailed interviews:

• Industrial-exposed cases (120 available): Take all 120.
• Other-exposure cases (1,880 available): Sample 100.
• Industrial-exposed non-cases (1,500 available): Sample 100.
• Other-exposure non-cases (46,500 available): Sample 80.

Because we have oversampled the small cells, weighting must be applied in analysis to recover correct association estimates; this is what the Cain & Breslow (1988) and later Flanders & Greenland (1991) methodologies handle. Hanley and colleagues (2005) provide worked examples of the adjusted odds ratio and its variance.

Practical Pitfalls

• Budget allocation between stages. Hanley and colleagues (2005) note that tools for optimal allocation have not advanced much in the past two decades; in practice, simulation can help determine the relative number of stage 1 and stage 2 subjects to maximise precision under a fixed budget.
• Variance estimation. The variance of the final estimate depends on both stages. Naive variances that ignore stage 2 sampling will be too small. Hanley and colleagues provide details for dichotomous covariates; software exists for more complex situations.
• Sampling fractions must be known. Weighting requires knowing exactly what proportion of each stage 1 cell was sampled at stage 2. If non-response or other losses change those fractions, the realised (not planned) fractions should be used.

Lesson 7 · Part 3 · HSCI 341

Controlled Studies

The experiments of epidemiology, where the investigator controls the exposure and random allocation breaks confounding by design.

Definition

What makes a trial randomised

A randomised controlled trial allocates participants to interventions using a formal chance-based mechanism, then follows them for outcomes.

Random allocation produces baseline comparability on both measured and unmeasured factors. That is the property no observational design can match.

Research phases

From pre-clinical to post-marketing

Pre-clinical → Phase 0 → Phase I

Lab and animal models → first-in-human (sub-therapeutic, n < 15) → safety in 20–100 healthy volunteers.

Phase II → Phase III → Phase IV

Efficacy signal in 100–300 patients → pivotal efficacy in 300–3,000+ → post-marketing surveillance over large populations.

Populations

Three nested groups

Trial objectives & comparators

Stating what you are testing

Good objective

Names the intervention, allocation design, and primary outcome. Limited in number to protect power and compliance.

Clinical equipoise

Randomisation is ethical only when genuine uncertainty exists. Where an effective standard treatment exists, it becomes the comparator.

Non-inferiority trials ask: is the new intervention no worse than the standard by more than a specified margin, delta? Choosing delta is one of the most consequential design decisions.

Specifying the intervention

Precise enough to replicate

• State type, dose, route, timing, and duration with enough detail that another investigator can replicate the work.
• A fixed protocol suits Phase III trials; a flexible protocol suits interventions with accumulated clinical experience.
• Monitor compliance: pill counts, biological assays, direct observation.
• Keep treatment assignment masked from clinical decision-makers wherever possible.

Carry forward

Next: the central design choices

• Randomisation balances measured and unmeasured confounders, conferring causal authority no observational design can match.
• Phased research establishes safety and efficacy incrementally before large-scale deployment.
• Populations and eligibility criteria set the generalisability of the trial before enrolment opens.

Introduction and Overview

Earlier lessons worked through the observational designs, including cross-sectional, cohort, case-control, ecological, and the hybrid variants. Every one of them measures exposure as it occurs naturally, and every one of them must spend effort defending against confounding. This lesson turns to the experimental alternative: when the investigator controls who is exposed via random assignment, confounding is broken by the design itself rather than by statistical adjustment. The three content sections move through an RCT in the order an investigator would build one: foundations and setup (this section), the central design choices around allocation, outcome measurement, sample size, and blinding (a later section), and finally the conduct, analysis, and reporting of the trial (a later section).

What Is a Randomised Controlled Trial?

A randomised controlled trial (RCT) is a planned experiment in which the investigator deliberately allocates participants to one or more interventions, then follows them to observe outcomes. Because the allocation is determined by the investigator (rather than by self-selection or by clinical circumstance), randomisation produces groups that are comparable on both measured and unmeasured factors at baseline. This is the property that gives the RCT its inferential power.

Throughout this lesson we follow the chapter convention of using RCT to describe any planned experiment evaluating products or procedures outside the laboratory. The terms clinical trial (often restricted to therapeutic products in clinical settings) and field trial (carried out in general population settings) are used interchangeably with RCT. The factor under investigation is called the intervention; the effect of interest is called the outcome; people or groups participating are called subjects or participants. The lineage of the controlled comparison reaches back to James Lind's 1753 shipboard trial of citrus for scurvy, but it was the 1948 MRC streptomycin trial that introduced formal random allocation as the design's defining feature.

CONSORT and Trial Registration

The Consolidated Standards of Reporting Trials (CONSORT) statement was developed to improve the quality of trial reporting. It was first published in 1996, updated in 2001, and again in 2010 (Schulz, Altman, & Moher, 2010). We will use its main headings as the structural template throughout this lesson; the full 25-item checklist appears in a later section. As of 2005, the International Committee of Medical Journal Editors required investigators to register their trials prior to participant enrolment as a precondition for publishing in member journals. The WHO operates an International Clinical Trials Registry Platform (ICTRP), although registration remains effectively voluntary in many jurisdictions.

The Phases of Clinical Research

While controlled trials are valuable for assessing a wide range of factors affecting health, one of their most common uses is to evaluate pharmacological products. Before any trial in humans, extensive pre-clinical studies are conducted in vitro (test tube or cell culture) and in vivo (animal) using wide-ranging doses to obtain preliminary efficacy, toxicity, and pharmacokinetic information.

Click any phase to see its purpose, typical sample size, and key design features.

Background, Objectives, and Trial Design

The objectives of a trial must be stated clearly and succinctly. A good objective describes the intervention, the allocation design (parallel, factorial, cross-over, etc.), and the primary outcome(s). Each trial should have a limited number of objectives plus, if needed, a small number of secondary outcomes. Increasing the number of objectives complicates the protocol, jeopardises compliance, and sacrifices statistical power.

Most trials contrast two groups, intervention and comparison, and are sometimes referred to as two-arm studies. Trials with more arms can be efficient when factorial designs are used (a later section). The comparison group might receive a placebo, no treatment, the usual treatment, or a different dose of the same product.

Participants: Defining the Study Group

Three nested populations must be distinguished in any trial:

Defining the Three Populations

• Target population: the population to which you want results to apply. Stating this explicitly helps ensure that conclusions remain practical and relevant.
• Source population: representative of the target population and consisting of eligible subjects from whom the study group is drawn. The setting and location of the source population should be described.
• Study group: the actual subjects who fit inclusion/exclusion criteria and agree to participate. Volunteers are unavoidable; how well they represent the source and target populations must be considered when extrapolating results.

Unit of Concern: Individuals or Clusters?

An early decision is the level at which the intervention will be applied. Some interventions can only be delivered to groups (e.g., medication added to drinking water; a school-wide curriculum). When the intervention is applied at the group level and the outcome is measured at the group level, this is a group-level study. When the outcome is measured on individuals within those groups, this is a cluster randomised study, which is discussed in a later section.

Eligibility Criteria

Specifying the Intervention

The nature of the intervention and how it is administered must be clearly defined, with enough detail that another investigator could replicate it. Interventions vary widely:

• Medical interventions (e.g., creatine supplementation, antibiotic regimens)
• Surgical techniques (e.g., single-layer vs. double-layer uterine closure)
• Devices or instruments (e.g., progressive lenses for presbyopia)
• Screening programmes (e.g., PSA testing for prostate cancer)
• Behavioural programmes (e.g., adolescent smoking cessation)

A fixed intervention (one with no flexibility) is appropriate for assessing new products in Phase III trials. A more flexible protocol is appropriate for products that have been in use long enough that some clinical judgment has accumulated. Whenever possible, the initial treatment assignment should remain masked so clinical decisions are not influenced by knowledge of group allocation. Clear instructions are critical when participants administer some or all of the intervention themselves (such as instructions for taking medication). A monitoring system should be in place to verify that the intervention is delivered as planned.

Introduction and Overview

An earlier section covered the up-front decisions: what an RCT is, what phase of clinical research it falls under, what the trial design is meant to test, and who gets included. This section turns to the four central design decisions that follow: how the outcome is measured, how large the sample needs to be to detect the effect, how participants are allocated to groups, and who is masked from the allocation. Each of these is a place where a poorly run RCT can lose its inferential advantage.

Measuring the Outcome

A controlled trial should be limited to one or two primary outcomes and a small number (one to three) of secondary outcomes. Having too many outcomes leads to multiple-comparisons problems (covered in a later section) and risks inflating the false-positive rate. Composite outcomes, which combine several events into a single measure, are sometimes used but remain controversial; for our purposes a limited number of primary and secondary hypotheses is preferred.

Outcome Scales

Choosing Clinically Relevant Outcomes

Outcomes that can be assessed objectively are preferred, but sometimes subjective outcomes are unavoidable (e.g., self-reported symptoms). When the outcome is not assessed by a near-gold-standard procedure, the impact of the intervention on the true outcome may differ from the impact on the surrogate. Intermediate outcomes (e.g., antibody titres in a vaccine trial) can illuminate mechanism but should not replace clinically relevant primary endpoints. Clinically relevant outcomes typically include:

• Diagnosis of a particular disease: requires a clear case definition
• Mortality: objective but still requires criteria for cause and time of death
• Severity scores: difficult to develop reliably
• Objective clinical measures (rectal temperature, blood biomarkers)
• Quality-of-life and other patient-reported outcome measures

Sample Size

The size of a trial is determined through formal sample-size calculations that incorporate the estimated intervention effect, Type I error rate, and Type II error rate. Power is conventionally set to 90 percent. The sample sizes do not need to be equal in both arms.

Sample Size for Cluster Randomised Trials

When subjects are randomised in clusters (families, schools, clinics), the analysis must account for within-cluster similarity, summarised by the intra-cluster correlation coefficient (rho or ICC) and the cluster size (m). The required sample size is inflated by the design effect:

The design effect tells you how many times larger a clustered sample must be to carry the same information as a simple random sample of unrelated individuals. The reason is that people in the same cluster tend to resemble one another, so a second person from a cluster you have already sampled adds less that is new than a wholly independent person would.

Even when rho is small, large clusters cause substantial inflation. Notably, the power of a cluster trial does not increase appreciably once the number of subjects per cluster exceeds 1/rho, so adding more individuals to existing clusters yields diminishing returns. Adding more clusters is often more efficient than adding more individuals per cluster.

Sequential and Adaptive Designs

set.seed(341)
n <- 200
arm <- factor(rep(c("control", "treatment"), each = n/2))

## (1) Continuous outcome: blood pressure
sbp <- rnorm(n, mean = ifelse(arm == "treatment", 128, 135), sd = 10)
t.test(sbp ~ arm)

## (2) Dichotomous outcome: cure (yes/no)
cure <- rbinom(n, 1, prob = ifelse(arm == "treatment", 0.45, 0.30))
tab <- table(arm, cure)
chisq.test(tab)
prop.test(table(arm, cure))            # with 95% CI for the difference

## (3) Time-to-event outcome: relapse (with right censoring)
library(survival)
time   <- rexp(n, rate = ifelse(arm == "treatment", 1/24, 1/14))
event  <- rbinom(n, 1, 0.7)
survdiff(Surv(time, event) ~ arm)         # log-rank test

Allocation of Study Subjects

Once enrolled, subjects must be allocated to interventions. Formal randomisation is the strongest method; without it, bias is very likely to distort findings (Schulz & Grimes, 2002a). Random allocation should occur as close to the start of the intervention as possible to minimise withdrawals between assignment and treatment, and concealment of the upcoming allocation from those enrolling participants is essential to prevent selection bias (Schulz & Grimes, 2002b).

It helps to keep two ideas apart. Allocation concealment protects the moment of assignment: it hides the upcoming allocation so that whoever enrols a participant cannot steer sicker or healthier people toward one arm. Blinding, discussed later, protects what happens after assignment, so that knowing the allocation does not colour treatment, behaviour, or outcome assessment. A trial can conceal allocation even when blinding is impossible, as in a trial of surgery versus physiotherapy.

Alternatives to Randomisation

set.seed(202509)                       # commit this seed before enrolment opens
N <- 120; arms <- c("Drug", "Placebo")

## (1) Simple randomisation
simple <- sample(arms, N, replace = TRUE)
table(simple)

## (2) Stratified by site (3 sites, 40 each)
strat <- unlist(lapply(c("Site_A", "Site_B", "Site_C"), function(s)
  paste(s, sample(rep(arms, 20)), sep = ":")))

## (3) Permuted-block randomisation (block size 4)
block <- unlist(replicate(N/4, sample(rep(arms, 2))))
head(block, 12)                             # every block of 4 has 2 of each arm

## Save the list - this is your audit trail
# write.csv(data.frame(id = 1:N, arm = block), "allocation_list_2025-09-01.csv",
#           row.names = FALSE)

The Family of Random Allocation Designs

Random allocation does not mean haphazard allocation. A formal process (a computer-based random number generator, sealed-envelope randomisation, or even a coin toss) must be used (Schulz & Grimes, 2002a). Click any design to see its features and an example.

Cluster Randomisation: Why It Is Less Efficient

Cluster randomised trials are statistically less efficient than individually randomised trials of the same total sample size (Campbell, Elbourne, & Altman, 2004). The clustering of subjects within groups must be accounted for in the analysis. The best follow-up scenario is to monitor all individuals for the duration of the study; if not, following a randomly selected cohort is the next most powerful approach. In some settings, repeated cross-sectional samples within each cluster must be used. Matched-cluster designs may be appropriate when the number of clusters is small, although “breaking the matches” can sometimes improve statistical efficiency.

Multicentre Trials

If an adequate sample is not available at one site, a multicentre trial is required. Within-centre and between-centre variances must be accounted for in design and analysis. Multicentre trials enhance generalisability (because of the broader geographic and clinical reach) and create opportunities to detect interaction effects across sites. For statistical efficiency, the number of subjects per centre should be approximately equal. Example 12.6 was conducted across five centres.

Masking (Blinding)

Blinding (or masking) refers both to the methodological principle of withholding information from individuals to prevent bias and to the specific procedures used to do so (Schulz & Grimes, 2002c). Terms can be used inconsistently in the literature, so the specific masking mechanisms always need to be described, and ideally pilot-tested in larger trials.

What Each Level of Blinding Prevents

The Role of Placebos

A placebo is a product indistinguishable from the active intervention, administered to the comparison group. In drug trials, the placebo is often the vehicle without the active ingredient. Even apparently inert placebos can have positive or negative effects (e.g., a placebo vaccine without antigen can still induce some immunity through adjuvant). These issues should be addressed before the trial begins. In some situations, blinding cannot be achieved with placebos alone, but masking should be implemented wherever feasible.

Introduction and Overview

Earlier sections settled the design. This section walks through what happens once the trial is running: how to track participants through follow-up, how to analyse the data (including the intention-to-treat principle and the special case of vaccine efficacy), and how to report the trial honestly via the CONSORT checklist. The reporting framework here connects directly back to the integrity material from an earlier lesson.

Follow-Up and Compliance

One of the most important practical issues is ensuring that all groups are followed rigorously and equally. The follow-up period must be long enough to capture all outcomes of interest. Some loss is inevitable through drop-out or non-compliance; for trials with long follow-up, the status of all subjects should be ascertained at regular intervals. The CONSORT statement strongly recommends a flow diagram showing participant numbers at allocation, intended intervention, protocol completion, and outcome assessment.

Strategies to Minimise Loss and Maximise Compliance

Statistical Methods and Analysis

Outcomes might be analysed on a continuous scale, as categorical (often dichotomous) data, or as time-to-event measurements. Time-to-event analyses can have greater power than simple occurrence-or-not in a defined window. Whatever the analysis, results should report both the effect size and its precision (typically a 95 percent confidence interval), and dichotomous outcomes should appear in both absolute (risk difference) and relative (risk ratio) terms.

Intent-to-Treat vs. Per-Protocol Analysis

This distinction is one of the most important in RCT analysis. Click the tabs to compare the two approaches.

Baseline Comparison and Covariate Adjustment

Analysis usually starts with a baseline comparison of group characteristics as a check on randomisation. This is an assessment of comparability rather than a statistical significance test. Differences between groups, even if not statistically significant, should be noted and may justify covariate adjustment.

For dichotomous outcomes, adjustment for covariates is recommended, ideally for strong predictors identified a priori; failing that, for variables predictive of the outcome in the trial data. Adjustment can substantially increase power or reduce required sample size. Adjustment for non-confounders does little harm provided they are not intervening variables (mediators).

For continuous outcomes, controlling for baseline (pre-intervention) values can substantially improve precision. This can be done either by analysing the change score (post minus pre) or by including baseline as a covariate. Either approach gains power, particularly when the baseline-to-follow-up correlation exceeds 0.5.

The Multiple Comparisons Problem

Multiple comparisons in RCTs arise from three sources: examining multiple outcomes, examining multiple subgroups, and performing periodic interim analyses during the trial. The problem is that the experiment-wise (family-wise) error rate is much larger than the per-test rate, making spurious “significant” findings increasingly likely as the number of tests grows.

The Bonferroni adjustment is the simplest fix: divide the desired experiment-wise alpha by the number of comparisons. It is conservative; less conservative procedures (Holm, Hochberg, Benjamini-Hochberg) are available in standard texts.

Sequential Analyses: When to Stop

Sequential design studies plan periodic analyses throughout the trial to allow early stopping for one of three reasons:

• Clear (and statistically significant) evidence of the superiority of one intervention over the other
• Convincing evidence of harm from the intervention (regardless of statistical significance)
• Little likelihood that the trial will produce evidence of an effect even if completed (futility)

Interim analyses must be pre-specified in the trial design; ad-hoc “peeking” inflates the false-positive rate and is regarded as a serious methodological breach.

Vaccine Trials: Direct, Indirect, and Total Efficacy

Standard RCT designs need modification when the intervention is a prophylactic against a communicable organism. The reason: an effective vaccine has effects on the vaccinated and on the unvaccinated, because vaccination reduces transmission. This means study subjects are not independent, an effect Hudgens and Halloran (2008) call interference.

Three Measures of Vaccine Efficacy

To get a fuller picture, epidemiologists distinguish three measures, each requiring information from at least two populations with different vaccination coverage. Use I_v for the incidence in the vaccinated and I_nv for the incidence in the unvaccinated; subscript A denotes the higher-coverage population, B the lower-coverage population.

Designing Vaccine Trials to Estimate All Three Measures

To estimate VE_d, VE_ind, and VE_tot, the design must include at least two comparable populations with different vaccination coverage. The recommended approach: in population A, randomise individuals to vaccine or placebo. In population B, leave everyone unvaccinated (or assign a lower coverage). The two populations must be (a) comparable in characteristics that affect the outcome, especially baseline transmission level, and (b) physically separated so subjects do not intermix.

An alternative when finding two similar populations is impractical is to exploit natural clustering, for example randomly assigning vaccination to half the children in a geographic area, then study spread within schools, recording the proportion of children at each school who were vaccinated. Riggs and Koopman (2005) and Longini and colleagues (1998, 2002) describe how to design and analyse such trials.

Reporting: The CONSORT 2010 Checklist

The CONSORT 2010 statement is the dominant reporting guideline for parallel-group randomised trials. Its 25 items align with the design and conduct topics covered throughout this lesson. The table below highlights items most relevant to the topics we have studied.

CONSORT extensions exist for cluster randomised trials, non-inferiority and equivalence trials, non-pharmacological treatments, herbal interventions, and pragmatic trials. Up-to-date references are available at www.consort-statement.org.