This glossary collects the key concepts, people, and ideas you will meet in this lesson. Use it as a reference while you work through the material, or as a review before assessments. Type in the search box to filter entries.

Introduction and Overview

An earlier lesson ended with a promise: cohort studies invert the case-control logic by sampling on the exposure rather than the disease, and that inversion lets us measure incidence directly without the rare-disease assumption that complicated odds-ratio interpretation. This lesson cashes that promise. Across seven content sections we walk from the basic logic of cohort design (this section), to the choice between risk-based and rate-based flavors that should now feel familiar from a later section, to the surprisingly difficult problem of measuring exposure in a longitudinal setting (a later section), to the practical questions of comparability, follow-up, outcome ascertainment, and analysis (a later section), and finally to the randomised controlled trial and other experimental designs, in which the investigator assigns the exposure (the last three sections). The unified-design discipline from an earlier lesson still applies; the lessons of an earlier lesson about pre-specified analysis plans apply with extra force, because cohort studies often run for decades and offer many opportunities for selective reporting.

What Is a Cohort Study?

The word cohort denotes a group of study subjects that has a defined characteristic in common. In epidemiological study design, that characteristic is usually exposure status. In a cohort study, we follow subjects from exposure to outcome (Grimes and Schulz, 2002).

Most frequently, the outcome is the occurrence of a specific disease, but cohort studies can also examine outcomes such as birth weight, body mass index, blood pressure, or quality of life. Subjects are usually individuals, but can also be groups (e.g., families).

The cohort design's modern reputation rests on a small number of landmark studies that the rest of this lesson will return to repeatedly: the Framingham Heart Study (Dawber, Meadors, & Moore, 1951), which gave epidemiology the term “risk factor” (Kannel et al, 1961); the British Doctors Study (Doll & Hill, 1954; Doll et al, 2004), which followed UK physicians for 50 years and pinned down the smoking–lung cancer link; the Whitehall II civil-servant cohort (Marmot et al, 1991), which exposed a graded socioeconomic gradient in chronic disease; the Nurses' Health Study (Colditz, Manson, & Hankinson, 1997); the multinational EPIC cohort (Riboli et al, 2002); and the recent generation of population biobanks, UK Biobank (Sudlow et al, 2015) and the Canadian Longitudinal Study on Aging (Raina et al, 2019).

Cohort and Case-Control Designs Compared

An earlier lesson built the case-control design, which starts from disease status and looks back to exposure. The table below sets the two designs side by side; read it as a guide to which direction of inquiry suits a given question.

Selecting the Study Sample (Participants)

How we select the cohort depends on what we know in advance. The three flip cards below name the standard choices, click each one and notice that the choice flows from the data already in hand, not from any abstract preference for one design over another.

In both two-cohort and single-cohort designs, after selecting subjects we (1) verify they meet inclusion criteria, (2) confirm exposure status, (3) ensure they do not yet have the outcome, then (4) follow them for a defined period and compare incidence between exposure groups.

Whichever cohort structure you pick, the next decision is whether the follow-up has already happened or whether you will be doing it as the study runs.

Prospective vs. Retrospective Designs

Cohort studies can be conducted either way, depending on whether suitable records already exist (Euser et al, 2009). The two tabs below put the trade-offs side by side.

Beyond the timing question is a structural one about the population itself: does its membership stay fixed for the duration of follow-up, or do people enter and leave? You met this distinction in an earlier lesson; it returns here as a more central concern, because cohort follow-up is what makes it operational.

Open vs. Closed Source Populations

The nature of the source population determines the appropriate design. This is a critical decision that affects everything from sample-size calculations to the choice of analytic methods. Read the table below as a checklist for matching disease type to design type, chronic outcomes almost always require open-population, rate-based handling, and a later section builds out exactly what that requires.

Key Examples

Three published examples bring the design choices we have just enumerated into one place. We will refer back to these throughout the lesson by number, so it is worth pausing on each one to identify which boxes the investigators ticked: prospective vs. retrospective, two-cohort vs. single, open vs. closed, risk-based vs. rate-based.

Record-Linkage Infrastructure for Canadian Cohort Studies

The retrospective and virtual cohorts described above depend on records that someone else has already collected. 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:

Stating the Study Objective

Each study should clearly specify:

• The target population (to which inferences will be made)
• The source population (from which the study sample, the participants, will be drawn)
• The unit of observation (individuals or groups)
• The exposure, the disease, and the follow-up period
• The setting (context or venue) of interest
• If biology is known: the amount or duration of exposure thought to cause disease, and the relevant time window for exposure (current vs. lifetime vs. historical)

The takeaways above name what changed conceptually compared with case-control designs. The worked example that follows makes the change concrete: because we sampled on exposure, the same kind of 2×2 table you met in earlier lessons now yields a risk ratio and an incidence rate ratio directly, no rare-disease assumption required.

The reflection below asks you to use the timing distinction in a concrete research scenario. After working through it and the knowledge check, a later section returns to the risk-vs.-rate split that the worked example just previewed and shows what each design buys, costs, and assumes.

Reflection

Introduction and Overview

An earlier section established what a cohort study is and named the design choices its investigators have to make. This section drills into the most consequential of those choices: whether to count events per person (risk) or events per unit of person-time (rate). The two designs share a 2×2 layout but differ in what they assume about the population and what they let you say about disease frequency. Sample-size planning, surprisingly, is a useful place to start, because the calculation is the same for both designs even when the analysis ends up being different.

Sample Size

Initial sample-size estimates are usually performed assuming an equal number of exposed and non-exposed subjects, and assuming the disease is measured by risk (Section 8.2.2). This approach is often sufficient for initial planning even if the population is open and a rate-based design must ultimately be used.

Risk-Based (Cumulative Incidence) Designs

This is the simplest form of cohort study, but several assumptions must hold:

• Exposure groups are defined at the start of the study and remain unchanged (fixed cohorts).
• The study groups are closed, all subjects must be observed for the full risk period.
• There should be few or no losses (some authors use >10% losses as a cut-point that casts doubt on validity).

2×2 Table: Risk-Based Cohort Design

We select n₁ exposed and n₀ non-exposed individuals (free of disease) from the source population, follow them for the full follow-up period, and observe a₁ exposed cases and a₀ non-exposed cases. The two risks of interest are:

HSCI 341 Lesson 4, Section 2 (Incidence: Risk and Rate) develops incidence risk with formula calculators, worked examples and the assumption of a closed population.

The two risks can be compared on two scales. The risk ratio divides one risk by the other; the risk difference (also called the attributable risk) subtracts them, giving the absolute difference in incidence between the exposed and unexposed groups:

In the hypothetical cohort from the worked example in an earlier section, RD = 0.080 − 0.030 = 0.050, or 50 extra cases per 1,000 exposed people over five years, alongside a risk ratio of 2.67. The absolute figure is the one that tells a health planner how many cases the exposure adds.

Risk-based designs are conceptually clean but operationally fragile, their assumptions break the moment people leave the cohort or the risk period extends beyond a few months. The rate-based alternative was developed precisely to handle the populations where those assumptions do not hold.

Rate-Based (Incidence Density) Designs

In many cohort studies, not every subject is under observation for the full risk period, especially when:

• The source population is dynamic (subjects enter and leave).
• The follow-up period is long.
• Subjects are added part-way through the biological risk period.
• A significant proportion of subjects withdraw from the study.
• Exposure status itself changes during the study.

In these situations, we cannot just count exposed and non-exposed subjects. Instead, we accumulate the amount of ‘at-risk time’ contributed by each subject in each exposure category. The denominator becomes person-time, not persons. For example, 10 people each followed for 2 years and 20 people each followed for 1 year both contribute 20 person-years, so this denominator credits every subject for exactly as long as we actually observed them.

2×2 Table: Rate-Based Cohort Design

Each subject contributes ‘at-risk’ time until they develop the disease, are lost to follow-up, or the study ends. The two rates of interest are:

You have now seen both designs from the inside. The next subsection puts them side by side; read it as a decision aid for matching design to research situation, not as a statement that one design is generally better than the other.

Comparing the Two Designs

Key Examples

The four examples below illustrate the design choice with real published studies. The first two are risk-based; the last two are rate-based. As you expand each, ask yourself why the investigators chose what they chose, in every case the source population's behaviour and the follow-up window's length will be doing most of the work.

The reflection below asks you to apply the choice from this section to a specific long-running occupational cohort. After working through it, a later section turns to a problem that stays mostly hidden in textbook treatments: how do you actually measure exposure when it can change over years or decades of follow-up?

Reflection

Introduction and Overview

Earlier sections set up the architecture of the cohort study and the choice of risk-vs.-rate design. Both treated “exposed” as if it were a fixed property of each subject. In real cohorts that is rarely true. People start smoking, quit, switch jobs, change diets; doses accumulate. This section is about how exposure is actually measured and handled when it can vary across years or decades of follow-up, the technical problem that distinguishes a working cohort study from a textbook one.

Why Exposure Measurement Matters

In cohort studies, the objective is to identify the consequences of a specific exposure factor. Exposures can range from study-subject characteristics (sex, age) to infectious or noxious agents, environmental exposures, or food-related factors. Exposures that can be manipulated are of special interest because they lead more directly to disease control.

Scales of Exposure Measurement

Exposure status can be measured on different scales, each with implications for design and analysis. The four flip cards below run from the simplest binary contrast up to compound measures that combine intensity and duration. The pattern to take away: more granular measurement makes the design better suited to detecting dose-response, but only if the underlying biology really has a graded effect.

The choice of measurement scale is independent of a second question: does the exposure stay fixed for the rest of the subject's life, or can it change?

Permanent vs. Non-Permanent Exposures

Both permanent and non-permanent exposures share a complication that becomes visible only when you start counting person-time: the gap between when exposure happens and when disease can plausibly result.

The Induction Period & Time-at-Risk

An important concept in cohort design is the induction period, the time after exposure is completed before disease can reasonably arise.

Changing Exposure Status

If exposure status changes during follow-up, an individual subject can contribute time-at-risk to both exposed and non-exposed categories:

• Previously non-exposed subjects contribute to the exposed category after the exposure threshold is reached.
• Previously exposed subjects contribute to the non-exposed category after any lag effects have ended.
• If a subject develops the disease, the exposure category assigned is the one they were in at the time the outcome occurred.

One last twist on the meaning of “exposure” is worth flagging before we move on, because it shows up surprisingly often in chronic-disease cohorts.

Disease as Exposure

Disease itself can serve as an exposure for other outcomes such as additional diseases, mortality, or quality-of-life measures. Lazo et al (2011) followed 11,000+ adults for 18 years using non-alcoholic fatty-liver disease (NAFLD) as the exposure. Those with NAFLD (whether or not they had elevated liver enzymes) had a similar mortality hazard ratio as those without NAFLD, an interesting null result.

Key Examples

The three published cohorts below illustrate the full range of exposure handling we just covered: a continuous diet exposure validated against multiple recalls, a multi-exposure design with biospecimens, and a multinational study that pushes from estimated relative risk to population-attributable fraction. Expand each one and notice which exposure-measurement decisions shape the rest of the design.

The reflection below puts the measurement-scale decision into a real research scenario. After working through it and the knowledge check, a later section closes the lesson by addressing the four practical questions that any cohort investigator faces once exposure is settled: keeping the groups comparable, managing the follow-up period, ascertaining outcomes, and analysing the data.

Reflection

Introduction and Overview

Earlier sections walked through the design choices: cohort architecture, risk-vs.-rate handling, and exposure measurement. With those locked in, the remaining work is operational. Four practical questions structure this section in turn: how do you make sure the exposed and non-exposed groups are comparable on the variables that aren't your exposure of interest, how long should you follow them, how do you confirm the outcome happened, and how do you analyse what you collect?

Ensuring Exposed & Non-Exposed Groups Are Comparable

If exposed and non-exposed groups are not comparable (that is, not exchangeable: you could not swap the exposed and non-exposed labels and still expect the same pattern of disease) with respect to factors related to both exposure and outcome, a biased (confounded) assessment results (Klein-Geltink et al, 2007).

Three approaches help ensure comparability:

Comparability addresses the cross-sectional baseline. The next question is what happens over time, specifically, how long the follow-up should last and what counts as time-at-risk for each subject.

Follow-Up Period

To enhance validity, the follow-up process must be as complete as possible and unbiased with respect to exposure. Achieving unbiased follow-up may require some form of blinding to exposure status:

• In prospective studies: assign follow-up tasks to researchers unaware of exposure status.
• In retrospective studies: keep record reviewers unaware of exposure status when possible.

Losses to follow-up are a perennial concern. Chang et al (2009) describe shared parameter models to reduce bias when losses are not randomly distributed.

Even careful follow-up only matters if the outcome itself is measured well. Cohort studies tend to be ambitious about exposure characterization but surprisingly casual about outcome ascertainment, and the next subsection is the corrective.

Measuring the Outcome

Although the most frequent outcome in cohort studies is the occurrence of a specific disease (measured as risk or rate), outcomes can also be:

• Ordinal: e.g., none, mild, moderate, severe.
• Continuous: e.g., birth weight, blood pressure, BMI, quality of life index (Example 8.2).

Harley et al (2011), for instance, examined polybrominated diphenyl ethers (PBDEs (a flame retardant) and infant birth weight, length, and head circumference) both exposure and outcome on continuous scales.

Diagnostic Criteria

Each study needs explicit protocols for determining outcome occurrence and timing. Clear diagnostic criteria minimise diagnostic errors. In retrospective studies, this can be challenging when only summary diagnostic information is available.

Incidence Requires Two Examinations

Strictly, measuring incidence requires:

1. An examination at the start of follow-up to ensure subjects do not yet have the disease.
2. A second examination to determine whether (and when) the disease developed.

If clinical diagnostic data are used, the incident date is usually based on the time of diagnosis, not the time of underlying disease occurrence, an important caveat for diseases with long subclinical phases. If subjects are screened at regular intervals, the time of disease occurrence is conventionally placed at the midpoint between examinations.

Multiple Outcomes

Comparability, follow-up, and outcome ascertainment are all design-stage decisions. The analysis stage is where those decisions translate into a quantitative result, and where pre-specified analysis plans (the EGAP-style discipline from an earlier lesson) earn their keep, because cohort data tempt almost limitless slicing.

Analysis

Time-Dependent Confounders

Gran et al (2010) describe a sequential Cox technique for data with time-dependent confounders, covariates that are affected by past exposure and predict future exposure and outcome (e.g., CD4 count when assessing HIV treatment effects).

Repeated Measurements

Xue et al (2010) explain how marginal and mixed-effect models can handle cohort data with repeated measurements of exposure and covariates, contrasting these with logistic and proportional hazards approaches.

The last operational concern, as in earlier lessons, is reporting. STROBE returns one more time, now with the items that matter specifically for cohort designs.

Reporting of Cohort Studies (STROBE)

The STROBE statement (von Elm et al, 2007) provides reporting guidelines for observational studies. Tooth et al (2005) elaborate criteria specific to cohort studies. These should be used both to plan and report studies, and to assess the validity of published work.

Appraising a Cohort Study: A Worked CASP Example

The comparability, follow-up and outcome principles of this section are what an appraisal checklist asks about. The CASP cohort checklist (Critical Appraisal Skills Programme, 2024) has 12 items: a focused issue (item 1), acceptable recruitment of the cohort (2), accurate measurement of the exposure and the outcome (3 and 4), identification of confounders and allowance for them (5a and 5b), follow-up that is complete and long enough (6a and 6b), the results and their precision (7 and 8), whether the results are believable (9), and whether they apply locally, fit other evidence and have implications for practice (10 to 12). The worked example below applies the items that carry most of the weight to a fictional excerpt, including a calculation of loss to follow-up.

Open each item to compare your own answer with a model answer.

Items 10 to 12 call for the wider literature and the local context, which Lesson 2 showed how to find and appraise. The JBI critical appraisal checklist for cohort studies (Moola et al., 2020) covers the same ground in eleven items, including whether participants were free of the outcome at the start, whether follow-up was complete, and whether strategies were used to address incomplete follow-up.

The reflection below is the section's exit ticket, a realistic review-the-paper prompt that requires you to use everything from this section. After working through it and the knowledge check, the next section turns from observational cohorts to the randomised controlled trial, the design that a cohort study most closely resembles.

Reflection

Section 5 of 7

Foundations of RCTs & Trial Set-Up

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

The opening section of this lesson described the cohort study as something close to a controlled trial without the randomisation of exposure, and the section on comparability quoted Hernan's observation that exchangeability is expected only when exposure is randomised. Every design in the first four sections measures exposure as it occurs naturally, so each must defend itself against confounding through restriction, matching, or analytic control. This section and the two that follow turn to the experimental alternative: when the investigator controls who is exposed through random assignment, the design itself breaks the link between exposure and confounders. The three sections move through a randomised controlled trial (RCT) in the order an investigator would build one: foundations and set-up (this section), the central design choices around outcome measurement, sample size, allocation, and blinding (the next section), and the conduct, analysis, and reporting of the trial (the section after that).

From Cohort Study to Randomised 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 and the next two sections we follow the textbook's 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.

An earlier lesson (Introduction to Observational Studies) placed experimental studies beside observational ones and ranked designs in a hierarchy of evidence. Randomisation leaves some biases untouched, and a later lesson (Design-Specific and Temporal Biases) examines what can go wrong after allocation, including failures of concealment and blinding, placebo and Hawthorne effects, non-adherence, and contamination.

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 and updated in 2001, 2010 (Schulz, Altman, & Moher, 2010) and 2025 (Hopewell et al., 2025), and a later section of this lesson sets out its checklist. Since 2005 the International Committee of Medical Journal Editors has required investigators to register their trials before participant enrolment as a precondition for publishing in member journals, and the WHO operates an International Clinical Trials Registry Platform (ICTRP). A later lesson (Integrated Appraisal of Epidemiological Research) uses CONSORT as a framework for appraising published trials, and an earlier lesson (Foundations of Epidemiology) discusses registration and preregistration as research-integrity reforms.

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.

Objectives, Comparators, and Clinical Equipoise

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 (see the next section). The comparison group might receive a placebo, no treatment, the usual treatment, or a different dose of the same product.

Participants: Target Population, Source Population, and Study Sample

Three nested populations must be distinguished in any trial:

Defining the Three Populations

These are the same target and source populations that the opening section of this lesson asked every cohort study to name when stating its objective; the figure above shows how they nest. What is distinctive in a trial is the study sample: it consists of the participants who meet the inclusion and exclusion criteria and agree to participate, so every participant is a volunteer. How well those volunteers 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 the next section discusses. A later lesson (Ecological and Group-Level Studies) returns to group-level designs in observational research.

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.

The reflection below asks you to set up a trial of your own using the decisions from this section. After working through it and the knowledge check, the next section turns to the central design choices: how the outcome is measured, how large the trial must be, how participants are allocated, and who is masked.

Reflection

Introduction and Overview

The previous 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. Too many outcomes create the multiple-comparisons problem introduced under “Multiple Outcomes” in an earlier section and inflate the false-positive rate; the next section shows how trials adjust for it. 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

An earlier lesson (Introduction to Observational Studies) urged the same care when a surrogate stands in for a clinically important outcome in observational designs.

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. An earlier section discussed sample-size planning for cohort studies, and a later lesson (Confounding and Statistical Inference) explains Type I and Type II errors and statistical power in more detail.

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 intracluster correlation coefficient (ICC, ρ) and the cluster size (m). The required sample size is inflated by the design effect:

For example, with ICC = 0.05 and m = 41, the design effect is 1 + 40 × 0.05 = 3.0, which triples the required sample size.

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.

The same design effect applies to surveys that sample clusters. HSCI 341 Lesson 2, Sections 4 and 5 (Sampling Distributions and Survey Analysis; Planning Sample Size), applies it to the analysis and the sample size of complex surveys.

Sequential and Adaptive Designs

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).

Concealment protects the moment of assignment, and blinding, discussed below, protects what happens after it; a later lesson (Design-Specific and Temporal Biases) examines both, along with the biases that arise when either fails.

Alternatives to Randomisation

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

A later lesson (Design-Specific and Temporal Biases) summarises the evidence that trials with inadequate blinding tend to report larger effects. The tabs below set out who is masked at each level and which biases each layer guards against.

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. The same later lesson describes placebo and nocebo effects and how large they can be.

The reflection below asks you to make these choices for a school-based trial. After working through it and the knowledge check, the next section follows the trial into motion: follow-up, analysis, vaccine trials, and reporting.

Reflection

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 back to the research-integrity material in an earlier lesson (Foundations of Epidemiology), including trial registration and selective outcome reporting.

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. The principles of complete, unbiased follow-up set out for cohort studies in an earlier section apply equally to trials, and a later lesson (Sampling, Selection Processes and External Validity) examines attrition bias in longitudinal studies.

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.

Intention-to-Treat and Per-Protocol Analysis

An intention-to-treat (ITT) analysis keeps every randomised participant in the group to which they were assigned, whatever they actually received, so it preserves the comparability that randomisation created and estimates the effect to expect when the intervention is used in practice. A per-protocol (PP) analysis is restricted to participants who complied with the protocol; it estimates the effect under ideal adherence, but it is likely to be biased because people who do not comply usually differ from those who do. ITT is therefore the primary analysis and PP a secondary one. A later lesson (Design-Specific and Temporal Biases) develops both analyses in its discussion of compliance and adherence bias.

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 same problem arose for cohort studies with many outcomes in an earlier section; trials add subgroups and interim looks as further sources.

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 designs, introduced in the previous section, 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. A later lesson (Ecological and Group-Level Studies) presents herd immunity as a property of populations that no individual possesses; vaccine trials need designs that can measure it.

In vaccine trials, direct, indirect and total effects describe herd effects: protection of the vaccinated person, protection that spreads to others, and their combination. The same three terms mean something different in mediation analysis (Lesson 7 and HSCI 410 Lesson 8), where they divide an exposure's effect into the part that runs through a mediator and the part that does not.

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 2025 Checklist

A later lesson (Integrated Appraisal of Epidemiological Research) introduces CONSORT's key requirements and its flow diagram as a framework for appraising published trials. CONSORT 2025 (Hopewell et al., 2025) is the dominant reporting guideline for parallel-group randomised trials. It updates CONSORT 2010, replacing its 25 items with 30 and adding a section on open science (registration, protocol, data sharing, funding and conflicts of interest). Its items align with the design and conduct topics covered in this and the previous two sections; the table below highlights those most relevant to the topics we have studied, numbered as in the 2025 checklist.

CONSORT extensions exist for cluster randomised trials, non-inferiority and equivalence trials, non-pharmacological treatments, herbal interventions, and pragmatic trials. They were developed for CONSORT 2010 and are used alongside the current statement until they are updated. Up-to-date references are available at www.consort-statement.org.

The reflection below asks you to design a trial of your own, drawing on all three trial sections. After working through it and the knowledge check, the final assessment draws on all seven sections of the lesson.

Reflection

Bringing It All Together

Where an earlier lesson looked backward from outcome to exposure, this lesson followed the arrow forward. An earlier section framed the cohort study as something close to a controlled trial without randomisation: pick a source population, classify exposure, follow people, and watch incidence accumulate. An earlier section then forced the central design choice, risk-based (cumulative incidence) for closed populations followed for a fixed time, or rate-based (incidence density) for open populations where person-time is the natural denominator, and connected each to its analytic toolkit (binomial / log-binomial vs. Poisson / survival).

Earlier sections zoomed in on the operational details that decide whether a cohort study survives appraisal. How exposure is scaled (dichotomous, ordinal, continuous, compound), whether it changes over time, how the induction period is handled, and how comparability is engineered through restriction, matching, and analytic control all determine whether the rate ratio you eventually report is estimating what you think it is. Blinded outcome ascertainment, careful handling of loss to follow-up, and STROBE-aligned reporting then turn a defensible design into a study other researchers can actually use.

The last three sections crossed from observational into experimental epidemiology. They set out the rationale for randomised controlled trials, the phases of clinical research, the mechanics of allocation and masking, sample size with the inflation factor for cluster trials, and the analytic and reporting standards (intention-to-treat, CONSORT 2025) that govern modern trial conduct. The shift is conceptually small, since the investigator now assigns the exposure that a cohort study can only classify, but methodologically large, because randomisation is what gives trials their causal authority.

The final reflection asks you to put the entire arc to work as a brief cohort proposal of your own; the 24-question assessment then checks the conceptual content of all seven sections directly. A later lesson will pull the camera back further to look at ecological and group-level designs (where the unit of analysis stops being the person) and the comparability and inference logic you just built will keep paying off there.

Final Knowledge Assessment

This assessment covers all sections of this lesson. You must score 100% to complete the lesson. Review the feedback after each attempt.