Target trial emulation

What this page answers

The five pages before this one all deal with problems of analysis: what to adjust for, how to match, how to weight, what to do when a confounder was never measured. This page deals with something that comes earlier — design.

The reason is an uncomfortable fact: the most serious errors in observational research are usually not the wrong choice of statistical method, but a research question that was never written down properly. “Does this drug work?” is not a question you can hand to an analysis, because it does not say: compared with what? Starting from when? Who counts as having taken it? Do three days count? What happens to people who stop?

In a randomised controlled trial those questions cannot go unanswered — you have to write the protocol before you can enrol the first patient. In a database study the data are already sitting there, you can start fitting models immediately, and so the questions get skipped. The consequences come back as bias.

Target trial emulation takes the trial’s discipline and moves it across: first write down the randomised trial you would run if ethics and money were no obstacle, fill in its seven components, and only then ask which people and which time points in the observational data can stand in for that protocol.

It is not a statistical method. It is a form to fill in. And what it repairs happens to be exactly what statistical methods cannot.

The seven components of a target trial

Of the seven, the first, third and fourth carry most of the weight, because they correspond to the three commonest and most damaging design errors.

Three design errors

Immortal time bias

If group membership can only be known after baseline (“did they start the drug during follow-up?”), then the stretch between baseline and starting the drug is time during which anyone assigned to the treated group could not have died — had they died, they would never have appeared in that group. Counting that stretch as treated survival hands the treated arm a span of guaranteed-alive follow-up out of thin air.

The censoring and the structure of survival data page demonstrates the mechanism in full with the real Stanford heart transplant data, so it is not repeated here. What the target trial framework adds is an explanation of why it happens: a trial cannot have this problem, because time zero is the moment of randomisation and the basis for allocation is already settled at that moment. Database studies commit it because the “time zero” cell was left blank.

Prevalent user bias

If people who are already taking the drug when the study window opens are enrolled into the treated group, what you have enrolled is people who have taken it for a while and come to no harm. The ones most susceptible — who developed a side effect after two weeks and stopped, or who already had the event — never make it into your cohort.

This is depletion of susceptibles, and it systematically makes the drug look safer than it is. It cannot happen in a trial, because a trial only enrols people who have not yet started. The corresponding fix is the new-user design: pin time zero to the moment treatment starts, and enrol only people who had not used the drug before that moment.

No active comparator (confounding by indication)

“Treated versus untreated” has a structural problem: the untreated are people a clinician judged did not need treating. They differ from treated patients in health status, in how often they see a doctor, in comorbidity, and in a great many things nobody wrote down.

An active comparator uses another drug for the same indication as the control. Both groups are people a clinician judged needed treatment, so the unmeasured factors that drive “treat or not” largely cancel between them. What remains is “why A rather than B”, which is usually a narrower and more measurable set of factors.

One simulated dataset, seven analyses

The setup: 8000 patients are followed in a database for 84 months, with the study window opening after month 24. Two drugs treat the same indication — drug A truly lowers the hazard of death to 0.80 (a hazard ratio), and drug B has no effect. There are two confounders:

• L, a recorded severity marker. It affects both whether someone is treated and which of the two drugs they get.
• U, an unrecorded measure of frailty. It affects whether someone is treated and it affects death, but it does not affect the choice between A and B.

The simulated data behave accordingly: treated and untreated people differ by 0.49 standard deviations of U, whereas users of A and users of B differ by only -0.082 of U — but by 0.65 of L. That contrast is the entire rationale for an active comparator design.

library(survival)
set.seed(20260822)

N <- 8000; RUN_IN <- 24; END <- 84; TRUE_HR <- 0.80

L <- rnorm(N)                                  # severity: recorded
U <- rnorm(N)                                  # frailty: not recorded
p_init <- plogis(-4.4 + 0.7 * L + 0.7 * U)     # monthly chance of starting some drug
is_A   <- rbinom(N, 1, plogis(0.8 * L))        # which drug, driven by L alone

alive <- rep(TRUE, N); init <- rep(NA_integer_, N)
onA <- rep(FALSE, N); onB <- rep(FALSE, N); death <- rep(NA_integer_, N)
for (m in 1:END) {
  start <- alive & is.na(init) & (runif(N) < p_init)
  init[start] <- m
  onA <- onA | (start & is_A == 1); onB <- onB | (start & is_A == 0)
  h <- 0.0055 * exp(0.6 * L + 0.6 * U + log(TRUE_HR) * onA)
  d <- alive & (runif(N) < pmin(h, 1))
  death[d] <- m; alive[d] <- FALSE
}

# -- The naive analysis: everyone alive when the window opens, grouped by
#    whether they ever used A. Prevalent users stay in (init <= 24) and the
#    clock starts at month 24 -> two errors stacked ----------------------
# -- The target trial version: enrol only people who start after the window
#    opens (new users), set time zero to the month they start, use people
#    starting B in the same period as the control arm (active comparator),
#    then apply IPTW on L ------------------------------------------------
ac <- data.frame(id = which(!is.na(init) & init > RUN_IN))
ac$arm  <- as.integer(is_A[ac$id] == 1)
ac$L    <- L[ac$id]
ac$time <- pmin(ifelse(is.na(death[ac$id]), END, death[ac$id]), END) - init[ac$id] + 1
ac$event <- as.integer(!is.na(death[ac$id]) & death[ac$id] <= END)
ac <- ac[ac$time > 0, ]

ps   <- fitted(glm(arm ~ L, data = ac, family = binomial()))
ac$w <- ac$arm / ps + (1 - ac$arm) / (1 - ps)
coxph(Surv(time, event) ~ arm, data = ac, weights = ac$w, robust = TRUE)

import numpy as np, pandas as pd, statsmodels.api as sm
from scipy.special import expit
from lifelines import CoxPHFitter

rng = np.random.default_rng(20260822)
N, RUN_IN, END, TRUE_HR = 8000, 24, 84, 0.80

L, U = rng.normal(size=N), rng.normal(size=N)
p_init = expit(-4.4 + 0.7 * L + 0.7 * U)
is_A = rng.binomial(1, expit(0.8 * L))

alive = np.ones(N, bool); init = np.full(N, -1); death = np.full(N, -1)
onA = np.zeros(N, bool)
for m in range(1, END + 1):
    start = alive & (init < 0) & (rng.random(N) < p_init)
    init[start] = m
    onA |= start & (is_A == 1)
    h = 0.0055 * np.exp(0.6 * L + 0.6 * U + np.log(TRUE_HR) * onA)
    d = alive & (rng.random(N) < np.minimum(h, 1))
    death[d] = m; alive[d] = False

idx = np.flatnonzero((init > RUN_IN))
ac = pd.DataFrame({"arm": (is_A[idx] == 1).astype(int), "L": L[idx]})
end = np.where(death[idx] < 0, END, np.minimum(death[idx], END))
ac["time"]  = end - init[idx] + 1
ac["event"] = ((death[idx] > 0) & (death[idx] <= END)).astype(int)
ac = ac[ac.time > 0]

ps = sm.Logit(ac["arm"], sm.add_constant(ac[["L"]])).fit(disp=0).predict()
ac["w"] = ac["arm"] / ps + (1 - ac["arm"]) / (1 - ps)
CoxPHFitter().fit(ac[["time", "event", "arm", "w"]], "time", "event",
                  weights_col="w", robust=True).print_summary()

“Analysed n” is the size of the dataset that row’s model actually ran on, not the size of the simulated cohort — change the design and the people who qualify change with it, so each row’s n and event count have to be read alongside its hazard ratio.

Reading down the ladder, each row changes exactly one thing:

• Row one is the analysis you see most often: of the 6777 people alive when the study window opens, 1685 who ever used drug B are dropped, and the remaining 5092 are grouped by whether they ever used drug A (people who used B are in neither arm, and that exclusion is itself something a paper should report). Of them, 1133 are prevalent users, already on the drug before the window opened, and everyone’s clock starts at the window. The estimate is 1.13 — the drug genuinely cuts the hazard of death by a fifth, and the naive analysis says it causes harm.
• Rows two and three differ in one thing only: time zero. They use exactly the same two groups of people. In row three the treated clock starts at the moment treatment begins, with no immortal time; in row two it starts at the study window, so those 21125 person-months of not-yet-treated time are counted as treated follow-up. The hazard ratio moves from 1.34 to 0.78. That gap is immortal time and nothing else.
• Row three to row four: adjusting for the measured L pulls 1.34 to 1.01. Better, but still far from the truth — because the unmeasured U is still there.
• Row three to row five: switch to an active comparator (new users of A against new users of B). Neither row adjusts for any covariate; changing the comparator alone moves the estimate from 1.34 to 0.93 — U cancelled between the arms without a single extra covariate being adjusted for. (Row four’s 1.01 is adjusted for L and so cannot be compared with row five: that would change two things at once.)
• Rows six and seven: deal with L as well, by regression adjustment or by IPTW, giving 0.79 and 0.78, with confidence intervals covering the true value of 0.80.

Time zero: three timelines

Time zero has to satisfy three conditions at once, and this is the framework’s most practical single check:

1. Eligibility is fully determined at that moment — no information that only arrives later.
2. The treatment strategy is assigned at that moment — you cannot wait to find out later which arm someone belongs to.
3. Follow-up begins at that moment — and all three must be the same instant.

Misalign them and bias follows. The new-user design works precisely because “the first dispensing of this drug” satisfies all three at once.

How this page ties the previous five together

Every cell of the seven-component form draws on one of the earlier pages:

There is also a diagonal connection: self-controlled designs are a different answer to the question of where the control comes from — inside the same person. They need no active comparator and no propensity score, because they never make a between-person comparison in the first place. That is where triangulation earns its keep: two designs whose assumptions barely overlap agreeing on an answer is more persuasive than any single analysis.

When a target trial cannot be emulated

One side effect of this framework is that it will tell you when a question cannot be answered with the data you have. Three common cases:

• Time zero is invisible in the data. Suppose you want to study the effect of taking up exercise, but no field records the day a person started — there is no time zero, and any grouping will be retrospective.
• Eligibility requires future information. “Patients who stayed on the drug for a year” can only be determined by surviving a year; that is not an eligibility criterion, it is an outcome.
• There is no reasonable active comparator. The drug is first in class, or the only possible control arm is no treatment. Unmeasured confounding by indication then cannot be escaped, and all you can do is quantify it honestly with a sensitivity analysis (an E-value, say).

“It cannot be answered” is a result too, and a far more valuable one than a structurally flawed analysis pushed through. It usually points to a different question, a different dataset, or a different design.

Why this page recommends no videos

As with self-controlled designs, this topic has no teaching-level video in any language — nothing at all in Chinese, and in English only three lecture recordings of between fifty-seven and eighty minutes. This site does not list videos of insufficient quality just to have some.

If you want to watch one, the most authoritative is Target Trial Emulation, given by Miguel Hernán himself (80 minutes); the other two are from Northwestern Feinberg (58 minutes) and NIHR RSS (57 minutes). All three assume you already know Cox models and IPTW, so they repay reading B6-01 through B6-05 first.

In print, the way in is Hernán and Robins’ original methodological paper (Am J Epidemiol 2016), together with the explanatory series that followed in JAMA and the BMJ.

Common misuses

Reproducing every number on this page

/opt/homebrew/bin/Rscript figures/scripts/B6-06-target-trial.R

Report a problem on this page