New-User Designs for Treatment Initiation

Why the Point of Initiation Matters

A treatment effect depends on who is compared and when follow-up begins. A person starting a medication today has a different treatment history from someone who has taken it for several years. Comparing these people as though both represented the same treatment condition can mix the effect of starting treatment with the consequences of having already received, tolerated, or persisted with it.

A new-user design defines eligibility before treatment initiation and starts follow-up at a shared index point: the date at which treatment is initiated for treated participants, and the corresponding assignment date for eligible untreated participants. “Shared” means the same position in each participant’s study timeline, not necessarily the same calendar date for everyone. The goal is to compare treatment strategies from a point at which prior treatment experience is restricted and baseline characteristics can be measured before assignment.

Specify the Initiation Comparison

Let \(E=1\) indicate that a person meets the eligibility criteria at the index date, and let \(N=1\) indicate that the person has no recorded use of the treatment during the prespecified washout period. Let \(A=1\) denote initiation at time zero and \(A=0\) denote the chosen alternative, such as not initiating at that point. Let \(L\) be measured covariates assessed before time zero, and let \(Y\) be a binary outcome assessed over a fixed follow-up horizon.

The target population is the eligible, treatment-naïve population, not all people who might ever receive treatment. For example, an initiation risk difference can be defined as \(E[Y^1\mid E=1,N=1]-E[Y^0\mid E=1,N=1]\). Here \(Y^a\) denotes the outcome under the specified baseline initiation condition \(a\), with subsequent care understood as part of the target strategy or policy. This contrast is not automatically the effect of sustained adherence; that requires a sustained-strategy estimand.

The alternative must be stated clearly. “No initiation at time zero” does not mean “never treated” unless the strategy explicitly says so. If people in the alternative group later start treatment, the interpretation depends on that subsequent-treatment policy. A new-user design sets up a meaningful time-zero comparison; it does not alone settle every later treatment decision.

Identification by Baseline Standardization

A new-user design improves the definition of the comparison, but observational initiation is not necessarily exchangeable. For a simple baseline initiation contrast, a common identification result uses consistency, conditional exchangeability, and positivity. Write \(Y^a\) for the potential outcome under baseline condition \(a\), and let \(L\) include the measured pre-initiation covariates needed to control confounding.

Proof. Conditional exchangeability gives \(E[Y^a\mid L,E=1,N=1]=E[Y^a\mid A=a,L,E=1,N=1]\) wherever the conditional treatment probability is positive. By consistency, the right-hand side equals \(E[Y\mid A=a,L,E=1,N=1]\). Average both sides over the distribution of \(L\) in the eligible, treatment-naïve target population. The law of iterated expectation gives $$ E[Y^a\mid E=1,N=1] = \int E[Y^a\mid L=l,E=1,N=1]\,dF(l\mid E=1,N=1), $$ and substituting the two equalities proves the result. Positivity ensures the observed conditional outcome mean is available for the target covariate strata. \(\square\)

This identifies a causal risk only under the stated assumptions. In particular, using a washout period does not guarantee exchangeability: clinical severity, treatment preference, or other causes of both initiation and outcome may remain unmeasured. Nor does the formula identify effects for people excluded by eligibility or the washout rule.

Why Prevalent Users Change the Comparison

A prevalent-user design includes people already taking treatment at cohort entry. Their treatment duration varies, and inclusion as a current user may depend on having survived, tolerated, and continued treatment up to that point. The resulting group is not simply a collection of people who would initiate treatment at the current index date. Restricting to new users avoids combining those different treatment histories in the treated group, although it cannot remove all selection or confounding.

The duration mixture can be stated precisely. Let \(C=1\) mean current use at observation, let \(D\) be duration of use, and let \(Y\) be a binary outcome measured at that observation. For a continuous duration variable, the law of total expectation gives $$ P(Y=1\mid C=1) = \int P(Y=1\mid C=1,D=d)\,dF(d\mid C=1). $$ If duration has a discrete distribution, the integral is a sum over its possible values. For continuous duration, individual values may have probability zero, so the integral—not an elementary sum of point probabilities—is the appropriate expression.

Derivation. Let \(I(Y=1)\) be the indicator of the outcome. Conditional expectation first on current use and duration, then on current use alone, yields $$ \begin{aligned} P(Y=1\mid C=1) &=E[I(Y=1)\mid C=1]\\ &=E\{E[I(Y=1)\mid C=1,D]\mid C=1\}\\ &=\int P(Y=1\mid C=1,D=d)\,dF(d\mid C=1). \end{aligned} $$ The final integrand is a version of the conditional probability, defined for \(F(d\mid C=1)\)-almost every \(d\). This identity describes the observed risk mixture; it does not assert that duration itself has a causal effect. \(\square\)

Diagnostics, Comparisons, and Limits

A new-user design is useful when the scientific question concerns starting treatment among people who are eligible and not recently exposed. Compared with a prevalent-user comparison, it gives treated participants a common treatment starting point and makes it possible to define baseline covariates before initiation. A randomized trial can provide the same time-zero structure while randomizing assignment; an observational new-user study must instead justify its adjustment for confounding. A comparison with noninitiators may also have substantial differences in treatment indication. The particular choice of comparator affects the causal question and must be made explicit.

Before interpreting results, check the design and data for signs that the intended comparison has failed:

• Insufficient treatment history. If the data do not capture the full washout period, some apparent new users may be prevalent users. State the lookback window and assess whether the data source can observe it.
• Misaligned time zero. Eligibility, covariates, initiation status, and outcome follow-up must refer to the same index point. Covariates measured after initiation may be consequences of treatment, not baseline confounders.
• Different eligibility rules. Applying different clinical criteria to initiators and noninitiators changes the populations being compared. Apply the same eligibility definition at each index date.
• Poor overlap. If some baseline profiles almost always initiate or almost never initiate, the positivity assumption may be implausible. Examine treatment probabilities and covariate distributions in both groups.
• Ambiguous subsequent treatment. If noninitiators later start treatment, specify how that behavior fits the target contrast. A baseline initiation comparison should not be described as an effect of never treating unless that is the strategy actually defined.

The design has important limits. A washout rule can misclassify prior use when records are incomplete, and a longer washout changes who is eligible. Excluding experienced users changes the target population, so results need not apply to people restarting treatment or continuing long-term therapy. Most importantly, aligning time zero and restricting prior use do not control unmeasured confounding, repair poor positivity, or guarantee that the observed treatment alternatives correspond to a clinically meaningful decision.