The Role of Instrumental Variables in Randomized Experiments

causal inference
randomized experiments
Published

June 11, 2026

6 min read

Background

Instrumental variables (IV) are econometricians’ pride. They underpin a great many scientific findings, and even the Nobel committee in Stockholm seems fond of them, judging by the laureates it picks. Yet their prominence outside academia is limited, and so I have not featured them on this blog as often as their importance warrants. Today I change that.

My goal here is to give an overview of how one can use instrumental variables inside randomized experiments. The material draws on the recent NEJM survey by Angrist, Gao, Hull, and Yeh (2025), which makes the case for IV methods in clinical trials. I keep the mathematical rigor to a minimum and shine the spotlight on the practical side of the ideas. A caveat worth stating up front: IVs are arguably even more powerful in the absence of randomization, where they rescue observational studies from confounding — but that is a separate topic for another day.

The setup that motivates everything below is simple and familiar to anyone who has run an experiment: randomized trials often fail to go according to plan. People assigned to treatment do not take it; people assigned to control find a way to get it anyway. IVs offer a principled way to recover causal effects when that happens.

Notation

Index participants by \(i\). Let

  • \(Y_i\) be the outcome.
  • \(Z_i \in \{0, 1\}\) denote random assignment to treatment, and
  • \(T_i \in \{0, 1\}\) denote the treatment actually received.

In a clean experiment these coincide, but with noncompliance they need not: a participant can have \(Z_i = 1, T_i = 0\) (assigned but untreated) or \(Z_i = 0, T_i = 1\) (a control who crossed over). The instrument is the randomized assignment \(Z_i\); the endogenous variable is the received treatment \(T_i\).

Following the potential-outcomes framework, write \(Y_i(1)\) and \(Y_i(0)\) for participant \(i\)’s outcome with and without treatment; the individual causal effect is

\[Y_i(1) - Y_i(0),\]

forever unobservable since only one of the two is realized.

Likewise, let \(T_i(z)\) be the treatment \(i\) would take under assignment \(z\). This last object lets us partition the population into four latent types:

  • Compliers take treatment when assigned and not otherwise: \(T_i(1) = 1, T_i(0) = 0\).
  • Always-takers take treatment regardless: \(T_i(1) = T_i(0) = 1\).
  • Never-takers refuse regardless: \(T_i(1) = T_i(0) = 0\).
  • Defiers do the opposite of their assignment — assumed away below.

Three quantities organize the analysis.

  1. The first stage is the effect of assignment (\(Z\)) on treatment (\(T\)) received, i.e. the difference in treatment rates between the assigned-treatment and assigned-control groups — also called compliance.
  2. The reduced form (or intention-to-treat, ITT, effect) is the effect of assignment (\(Z\)) on the outcome (\(Y\)).
  3. The local average treatment effect (LATE) is the average causal effect among compliers.

The whole framework rests on four assumptions:

  1. random assignment of \(Z_i\);
  2. a first-stage (relevance) condition — assignment must actually move treatment, so compliance is non-zero;
  3. monotonicity — assignment never pushes anyone away from treatment, which rules out defiers; and
  4. the exclusion restriction — assignment affects the outcome only through treatment receipt, never directly.

A Closer Look

Use Case #1: Noncompliance

In a trial where everyone complies, \(T_i = Z_i\), and the difference in mean outcomes by assignment is the average treatment effect. Noncompliance breaks this.

Suppose treatment effects are constant and equal to \(\beta\), so that

\[Y_i = Y_i(0) + \beta T_i.\]

Then a little algebra on the assignment-based comparison gives

\[ \underbrace{\text{ITT effect}}_{\text{reduced form}} = \beta \times \underbrace{\text{Compliance}}_{\text{first stage}}. \]

The intuition is that the ITT effect gets diluted: when only a fraction of those assigned actually take treatment, the assignment-versus-assignment comparison mixes in untreated people on the treatment side and crossovers on the control side, shrinking the apparent effect toward zero. If compliance is, say, \(0.4\), the ITT understates the true effect by more than half.

The fix falls right out of the identity. Dividing the reduced form by the first stage recovers the effect:

\[ \beta = \frac{\text{ITT effect}}{\text{Compliance}} = \frac{\text{reduced form}}{\text{first stage}}. \]

This ratio of differences in means is the heart of IV analysis — the Wald estimator. When effects are heterogeneous, the LATE theorem (Imbens and Angrist, 1994) tells us this same ratio identifies not some universal \(\beta\) but the average effect for compliers:

\[ \frac{\text{ITT effect}}{\text{Compliance}} = \mathbb{E}\big[Y_i(1) - Y_i(0) \mid \text{complier}\big]. \]

Use Case #2: Selection Bias

The second problem IVs solve is subtler, and it is where practitioners most often go wrong. Faced with noncompliance, the tempting move is a per-protocol or as-treated analysis: just compare people by the treatment they actually received, \(T_i\). The trouble is that \(T_i\) is not randomized. The people who comply, cross over, or refuse differ systematically, so comparing by treatment received reintroduces exactly the confounding that randomization was designed to eliminate.

The IV approach sidesteps this entirely by comparing groups defined by randomized assignment \(Z_i\), not by \(T_i\). The comparison is apples-to-apples — the complier subpopulation on the treated side is statistically identical to the complier subpopulation on the control side, differing only in the luck of the draw. The estimate is a per-protocol effect, but one purged of selection bias. As a bonus, although individual compliers cannot be identified, their average baseline characteristics can be computed, letting the analyst check how representative they are of the broader patient population.

Bottom Line

  • Instrumental variables are ubiquitous in academic econometrics and applied microeconomics; their footprint in industry remains comparatively small.
  • Randomized experiments do not always go according to plan — noncompliance and crossovers are common in pragmatic and clinical trials.
  • IVs come to the rescue for two distinct, thorny problems: noncompliance and selection bias.
  • The price is interpretational: IV identifies the LATE, an effect specific to the compliers induced by the instrument — not necessarily the average effect for the whole population. Whether that is the estimand you want is a question worth asking before you run the regression.

Where to Learn More

The two foundational papers are Imbens and Angrist (1994), which introduced the LATE theorem, and Angrist, Imbens, and Rubin (1996), which recast IV estimation in the potential-outcomes language used throughout this note. For a complete and famously readable treatment, Angrist and Pischke’s Mostly Harmless Econometrics (2009) remains the standard reference. The clinical-trials framing here follows Angrist, Gao, Hull, and Yeh (2025), an accessible survey aimed at medical researchers that I recommend to anyone who wants to see these ideas applied end-to-end on a real trial.

References

  • Angrist, J. D., Gao, C., Hull, P., & Yeh, R. W. (2025). Instrumental variables in randomized trials. NEJM Evidence, 4(4).

  • Angrist, J. D., Imbens, G. W., & Rubin, D. B. (1996). Identification of causal effects using instrumental variables. Journal of the American Statistical Association, 91(434), 444–455.

  • Angrist, J. D., & Pischke, J.-S. (2009). Mostly Harmless Econometrics: An Empiricist’s Companion. Princeton University Press.

  • Imbens, G. W., & Angrist, J. D. (1994). Identification and estimation of local average treatment effects. Econometrica, 62(2), 467–475.