Cohort Design

Cohort Design, Time Zero and Risk Measures in Economic Models

In a cohort study, investigators record who is exposed to a treatment or risk factor, follow everyone forward in time and compare how often the outcome occurs in each group. Because exposure is fixed before the outcome happens, a cohort measures risks and rates directly, making it a common source of baseline event rates, resource use and real-world treatment comparisons for economic models. The start of follow-up (time zero) matters, and in an illustrative example below a timing error almost doubles an apparent cost saving.

How a cohort study is assembled

The STROBE explanation and elaboration paper describes the sequence, in which investigators obtain information about people and their exposures at baseline, let time pass, and then assess the occurrence of outcomes. Comparisons are usually made between exposed and unexposed people or across categories of exposure. The CDC's Principles of Epidemiology separates this from an experiment, because the investigator observes exposure status rather than assigning it, and the unexposed group supplies the expected amount of disease in the absence of exposure.

The NICE real-world evidence framework (ECD9) defines cohort studies as studies in which people are identified by their exposures and outcomes are compared during follow-up; observational data can also form an external control for a single-arm trial.

Time zero and aligning eligibility, assignment and follow-up

Hernán and colleagues describe many observational analyses as attempts to emulate a hypothetical pragmatic randomised trial, the target trial. In a trial, time zero is the moment a person meets the eligibility criteria and is assigned to a treatment strategy. The NICE framework applies the same rule to cohorts, so follow-up should ideally begin when all eligibility criteria are met and the intervention is assigned, or just after.

Hernán and colleagues show that bias can follow when these moments drift apart, even with full adjustment for confounding. Enrolling people already using a drug restricts the analysis to those who stayed under follow-up until the reset start. If treatment groups are defined by what people did after time zero, part of the treated group's follow-up becomes event-free by construction.

Prospective and retrospective cohorts

In the CDC's description, a prospective cohort enrols participants as the study begins and follows them forward, while in a retrospective cohort both the exposure and the outcomes have already occurred when the study starts. The labels say little about quality. STROBE recommends that authors refrain from simply calling a study prospective or retrospective because the terms are ill defined, and asks them to describe exactly how and when data were collected. The NICE framework advises against the distinction because it does not necessarily convey information about study quality. A cohort reconstructed from administrative data or an electronic health record faces the same threats from confounding and loss to follow-up as one recruited for the purpose.

Risks, rates and the ratios built from them

A cohort counts outcomes in each group from time zero onwards. STROBE notes that incidence can be expressed as the proportion of people developing the outcome over a period, the cumulative incidence, or as a rate per unit of person-time, and that "relative risk" can mean a ratio of either. With complete follow-up over a fixed period, the risks and their ratios are as follows.

$$\hat{R}_g = \frac{E_g}{N_g}, \qquad \widehat{RD} = \hat{R}_1 - \hat{R}_0, \qquad \widehat{RR} = \frac{\hat{R}_1}{\hat{R}_0}$$

where $g = 1$ is the treated or exposed group and $g = 0$ the comparison group, $E_g$ is the number of people with the event, $N_g$ is the number followed from time zero, $\hat{R}_g$ is the estimated risk, $\widehat{RD}$ is the risk difference and $\widehat{RR}$ is the risk ratio. When follow-up varies between people, the rate uses person-time, as follows.

$$\hat{I}_g = \frac{E_g}{T_g}, \qquad \widehat{IRR} = \frac{\hat{I}_1}{\hat{I}_0}$$

where $T_g$ is the total person-time at risk in group $g$, $\hat{I}_g$ is the incidence rate and $\widehat{IRR}$ is the incidence rate ratio.

The Cochrane Handbook (chapter 6) notes that the importance of a risk difference depends on the underlying risk, and that the number needed to treat is obtained from it. STROBE explains that person-time and life-table methods assume that, among people still free of the outcome when observation ends, follow-up time is unrelated to their chance of the outcome. Loss to follow-up concentrated in exposed or high-risk people breaks this assumption, which STROBE calls informative censoring.

Confounding and the designs that reduce it

In routine care, clinicians choose who receives a treatment, so treated and untreated people differ in baseline risk. Yoshida and colleagues call this confounding by indication. Cyclooxygenase-2 inhibitors, preferred for people at high risk of gastrointestinal bleeding, can appear to cause bleeding. Adjustment, for example with a propensity score, handles measured differences only, and the ISPOR-SMDM state-transition modelling report states that effectiveness taken from observational studies must be adjusted for confounding.

Two design choices act on the comparison itself. An active comparator design compares the drug of interest with another drug used for the same indication rather than with non-users, who, Yoshida and colleagues note, include people with no indication for treatment or with contraindications to all of it. A new-user design starts follow-up at treatment initiation, so pretreatment characteristics can be measured as baseline covariates and early adverse events are captured. The NICE framework prefers both, since active comparators reduce the risk of confounding by indication, and new-user designs carry a lower risk of selection bias because prevalent users have by definition stayed on treatment and survived for a period.

Suissa defines immortal time as a span of cohort follow-up during which, because of the exposure definition, the outcome could not occur, and shows that the resulting bias in the rate ratio grows in proportion to its duration. Hernán and colleagues note that it cannot arise in the intention-to-treat analysis of a true trial.

How cohort evidence enters economic evaluation

The NICE framework lists designing, populating and validating economic models among the uses of real-world data, including baseline event rates, transition probabilities, resource use and costs. Its examples include Clinical Practice Research Datalink data on baseline COPD exacerbation rates in the NICE COPD guideline (NG115). It also cautions that background event rates from trials may over- or underestimate rates in the target population because of selective recruitment, one reason a population cohort can be the better source of baseline risk.

The ISPOR-SMDM report recommends deriving transition probabilities from the most representative data sources for the decision problem and converting probabilities between time units through rates. A cohort reports risk over its own follow-up, so a model with annual cycles needs a conversion. Assuming a constant rate, the conversion is as follows.

$$r = \frac{-\ln(1 - R_t)}{t}, \qquad p = 1 - e^{-r}$$

where $R_t$ is the cumulative risk over $t$ years, $r$ is the constant annual rate and $p$ is the annual transition probability; rate-to-probability conversion has its own page.

A cohort study differs from a cohort model such as a Markov cohort model. The study follows real people through observed time, while the model runs a hypothetical population through modelled states. Model outputs inherit any bias in the cohort estimates that feed them.

Worked example of a new-user cohort and an immortal time error

All numbers are illustrative. A routine-data cohort compares two drugs for the same chronic condition with a new-user, active-comparator design. Time zero is the first prescription; 2,000 people start drug A and 3,000 start drug B, all are followed for two years with no losses, and the outcome is hospital admission for heart failure. The groups are assumed comparable after adjustment.

1. Effect measures. There are 120 admissions with drug A and 240 with drug B, so the risks are 120 / 2,000 = 0.06 and 240 / 3,000 = 0.08. The risk difference is 0.06 − 0.08 = −0.02, the risk ratio is 0.06 / 0.08 = 0.75 and the number needed to treat for two years to prevent one admission is 1 / 0.02 = 50.

2. Annual model inputs. For drug B, −ln(0.92) = 0.08338, so the annual rate is 0.04169 and the annual probability is 1 − e^(−0.04169) = 0.0408. For drug A, −ln(0.94) = 0.06188, giving a rate of 0.03094 and an annual probability of 0.0305.

3. Costs. At an illustrative GBP 3,000 per admission, 1,000 people treated with drug A rather than drug B avoid 1,000 × 0.02 = 20 admissions over two years, saving 20 × GBP 3,000 = GBP 60,000.

4. An immortal time error. A second analysis defines drug A users as people who filled three prescriptions, which takes six months, but still starts follow-up at the first prescription. Forty of drug A's 120 admissions happened before a third fill, so those 40 people never qualify and drop out of group A; everyone without an early admission is assumed to reach the third fill. Drug A now shows 80 admissions among 1,960 people, a risk of 0.0408, a risk ratio of 0.0408 / 0.08 = 0.51 and a risk difference of 0.0408 − 0.08 = −0.0392.

5. Effect on the economics. The biased analysis implies an absolute reduction of 1,000 × 0.0392 = 39.2 admissions per 1,000 people, a saving of 39.2 × GBP 3,000 = GBP 117,600, and an annual probability for drug A of 1 − (1 − 0.0408)^(1/2) = 0.0206 instead of 0.0305.

Interpretation. Only the exposure definition changed between steps 1 and 4. Drug A's first six months were made event-free by construction, which cut the risk ratio from 0.75 to 0.51 and almost doubled the apparent saving per 1,000 people. A model built on the second analysis would overstate the value of drug A, and sensitivity analysis on its inputs would not reveal the cause.

Related designs and where each applies

A case-control design starts from people with and without the outcome and compares their earlier exposures. It suits rare outcomes, but the NICE framework generally does not recommend case-control studies within existing databases because they use less information than cohort studies.

A randomised controlled trial assigns treatment, and the NICE framework calls it the preferred design for causal effects because randomisation makes differences in known and unknown baseline characteristics a matter of chance. Cohort studies are one kind of observational study and a common route to real-world evidence.

Where cohort evidence misleads a model

Cohort studies observe care in which treatment is chosen rather than assigned. The points below are common sources of error when their results feed an economic model.

• An adjusted estimate is a causal effect only if the important confounders were measured and handled; Hernán and colleagues note that success in adjusting for all confounding is never certain.
• A dramatic protective effect in routine data is a signal to check time zero and the exposure definition.
• Ratios without absolute risks are of limited use to a model. STROBE cites a survey in which absolute risks were given in 62% of trial abstracts reporting a ratio measure but in only 21% of cohort study abstracts.
• A comparison with non-users answers a different question from a comparison with current practice.

Sources

• Centers for Disease Control and Prevention. Principles of Epidemiology in Public Health Practice, third edition. Lesson 1, section 7: Analytic epidemiology. Published October 2006, last reviewed May 2012. https://archive.cdc.gov/www_cdc_gov/csels/dsepd/ss1978/lesson1/section7.html
• Hernán MA, Sauer BC, Hernández-Díaz S, Platt R, Shrier I. Specifying a target trial prevents immortal time bias and other self-inflicted injuries in observational analyses. Journal of Clinical Epidemiology. 2016;79:70-75. https://doi.org/10.1016/j.jclinepi.2016.04.014
• Higgins JPT, Li T, Deeks JJ, editors. Chapter 6: Choosing effect measures and computing estimates of effect. In: Higgins JPT, Thomas J, Chandler J, et al., editors. Cochrane Handbook for Systematic Reviews of Interventions, version 6.5. Cochrane; 2024. https://www.cochrane.org/authors/handbooks-and-manuals/handbook/current/chapter-06
• National Institute for Health and Care Excellence. NICE real-world evidence framework (ECD9). Published 23 June 2022, last updated September 2025. https://www.nice.org.uk/corporate/ecd9
• Siebert U, Alagoz O, Bayoumi AM, et al. State-transition modeling: a report of the ISPOR-SMDM Modeling Good Research Practices Task Force-3. Value in Health. 2012;15(6):812-820. https://doi.org/10.1016/j.jval.2012.06.014
• Suissa S. Immortal time bias in pharmaco-epidemiology. American Journal of Epidemiology. 2008;167(4):492-499. https://doi.org/10.1093/aje/kwm324
• Vandenbroucke JP, von Elm E, Altman DG, et al. Strengthening the Reporting of Observational Studies in Epidemiology (STROBE): explanation and elaboration. PLoS Medicine. 2007;4(10):e297. https://doi.org/10.1371/journal.pmed.0040297
• Yoshida K, Solomon DH, Kim SC. Active-comparator design and new-user design in observational studies. Nature Reviews Rheumatology. 2015;11(7):437-441. https://doi.org/10.1038/nrrheum.2015.30