Why the Assumptions Must Work Together
An encouragement can shift whether people receive a treatment without assigning treatment perfectly. Instrumental variables use that shift to learn about a causal effect, but no single assumption does all the work. Relevance supplies a change in treatment receipt; independence makes the encouragement groups comparable; exclusion rules out a separate route from encouragement to outcome; and monotonicity determines how to interpret the people whose treatment changes.
The target is generally not the average treatment effect for everyone. Under the assumptions below, it is the average treatment effect for compliers: people who receive treatment when encouraged and do not receive it when not encouraged. That population-specific interpretation is the central point of this synthesis.
Potential Outcomes and the Joint Identification Result
Let \(Z\in\{0,1\}\) denote a binary instrument, where \(Z=1\) is the encouragement, and let \(D\in\{0,1\}\) denote treatment receipt. For each person, \(D(z)\) is the treatment receipt that would occur under instrument value \(z\). Let \(Y(d)\) be the outcome that would occur under treatment value \(d\). The observed data satisfy \(D=D(Z)\) and \(Y=Y(D)\). These equalities are consistency statements: the observed treatment and outcome agree with the potential outcomes for the conditions actually experienced.
The usual identification argument requires the following conditions, stated for the population under study. It also presumes that the instrument, treatment, and outcome are well-defined, and that one person's instrument assignment does not change another person's treatment or outcome.
- Relevance: \(E[D\mid Z=1]\ne E[D\mid Z=0]\). The encouragement changes the population probability of treatment receipt.
- Independence: \(Z\) is independent of the potential treatments and outcomes: \(Z\perp (D(0),D(1),Y(0),Y(1))\). Random assignment of the encouragement is one design that supports this condition.
- Exclusion: the instrument affects the outcome only through treatment receipt. In potential-outcome notation, the outcome under instrument value \(z\) and treatment value \(d\) is \(Y(d)\), not a separate \(Y(z,d)\).
- Monotonicity: \(D(1)\ge D(0)\) for every person. Encouragement may move some people into treatment, but it does not cause anyone who would otherwise be treated to forgo treatment. Thus there are no defiers.
Together, these conditions give a precise interpretation to the ratio of the observed outcome contrast to the observed treatment contrast:
The denominator must be nonzero, which is relevance. The logic of the result is that independence makes the two instrument groups comparable in their potential outcomes and treatment responses. Exclusion means that any outcome contrast between those groups must come through treatment receipt. Under monotonicity, always-takers and never-takers have the same treatment receipt under either instrument value, so their treatment does not change with encouragement. Only compliers change treatment. Consequently, the outcome contrast is generated by treatment changes among compliers, and the treatment contrast reflects those same changes. Dividing the contrasts identifies the average effect for that group.
This argument also shows why the assumptions cannot be treated as interchangeable. Relevance without independence can compare different kinds of people. Independence without exclusion can leave a direct effect of encouragement in the outcome contrast. Exclusion without monotonicity permits treatment changes in opposite directions, so the contrast need not represent the effect for compliers alone.
Worked Example: All Four Assumptions Point to the Complier Effect
Suppose a hypothetical randomized encouragement is offered to 1,000 eligible people, with 500 assigned to each instrument group. Treatment receipt is recorded for everyone. The treatment rate is 0.40 in the \(Z=0\) group and 0.70 in the \(Z=1\) group. The mean outcome, measured in symptom-score points, is 12.0 for \(Z=0\) and 13.8 for \(Z=1\). Assume higher scores are worse.
Relevance: the treatment contrast is \(0.70-0.40=0.30\), so encouragement is associated with a 30-percentage-point increase in treatment receipt. The relevance condition holds in these data.
Independence: because encouragement was randomly assigned, assignment is independent of potential treatment receipt and potential outcomes by the design, apart from chance imbalance in this finite sample. Randomization supports independence; the observed rates alone do not prove it.
Exclusion: suppose the encouragement is only a private reminder to discuss and obtain the treatment, and does not otherwise change symptom scores. That design argument supports exclusion. If the reminder also provides counseling that changes symptoms without treatment, exclusion would not hold.
Monotonicity: suppose the reminder cannot deter anyone who would otherwise receive treatment. This supports the no-defiers condition, though the individual counterfactual treatment choices cannot be observed together to verify it person by person.
If these assumptions are accepted, the estimated outcome contrast is \(13.8-12.0=1.8\) symptom-score points. The ratio is
The estimate is an average increase of 6.0 symptom-score points caused by treatment among compliers, with the direction interpreted according to the scale: treatment worsens the score if higher values are worse. It is not automatically the effect for all eligible people. The arithmetic does not establish the assumptions; the randomization and design arguments are what make this causal interpretation plausible.
What Each Violation Changes
Worked Example: A Direct Effect Breaks Exclusion
Consider a hypothetical setting in which the encouragement increases the treatment rate by 0.30. Suppose treatment improves the outcome by an average of 4 units among compliers, so its contribution to the outcome contrast is \(0.30\times(-4)=-1.2\) units. Now suppose the encouragement also directly improves the outcome by 0.6 units, for example by providing useful advice even to people who do not take treatment. The observed outcome contrast is then \(-1.2+0.6=-0.6\) units.
The ratio of contrasts would be
This is not the complier treatment effect of \(-4\) units. The direct improvement of 0.6 units has entered the numerator, even though it is not caused by treatment receipt. The calculation is arithmetically correct, but the exclusion condition needed to interpret it causally is false.
Worked Example: Dependence Between Encouragement and Baseline Risk
Suppose, in a hypothetical nonrandomized setting, the \(Z=0\) group has a mean untreated outcome of 10 points and a treatment rate of 0.20, while the \(Z=1\) group has a mean untreated outcome of 14 points and a treatment rate of 0.50. Assume treatment has no effect on anyone, exclusion holds, and there are no defiers. The higher-risk group is more likely to receive encouragement.
The observed treatment contrast is \(0.50-0.20=0.30\). Because treatment has no effect, the outcome contrast is the baseline-risk difference, \(14-10=4\) points. The ratio is \(4/0.30=13.33\) points, although the true treatment effect is zero for every person.
This example violates independence: instrument assignment is related to potential outcomes. Relevance and exclusion do not repair that problem. The outcome contrast includes the baseline difference between groups, so it cannot be attributed solely to treatment changes induced by encouragement.
Worked Example: Defiers Change the Population Contrast
Consider a hypothetical population with 30% compliers, 10% defiers, and the remaining 60% divided between always-takers and never-takers. Suppose independence and exclusion hold. The average treatment effect is 0.8 outcome units among compliers and 0.2 units among defiers. The treatment contrast is \(0.30-0.10=0.20\): compliers increase receipt under encouragement, while defiers decrease it.
The outcome contrast contributed by compliers is \(0.30(0.8)=0.24\) units. The defiers contribute \(-0.10(0.2)=-0.02\) units because their treatment moves in the opposite direction. The total outcome contrast is therefore \(0.24-0.02=0.22\) units. Dividing gives
That value is not the complier effect of 0.8 units. With defiers, the contrast combines effects from treatment changes in opposite directions. Monotonicity is what rules out this signed mixture and allows the target to be described as the complier average treatment effect.
Diagnostics, Alternatives, and Limits
The assumptions differ in how much the observed data can tell us about them. Relevance can be assessed by estimating the difference in treatment rates across instrument groups; a very small difference signals a weak empirical shift and unstable ratio estimates. But observed data cannot generally reveal whether assignment is independent of all potential outcomes, whether the instrument has no direct effect, or whether no individual is a defier. Those claims require design knowledge and substantive argument. A favorable comparison of observed baseline characteristics may support the randomization story, but it does not prove independence for unobserved characteristics or potential outcomes.
A randomized trial that assigns treatment directly avoids the incomplete-uptake problem if assignment determines receipt, and can identify a broader treatment effect under its own assumptions. In an encouragement design, comparing outcomes by encouragement assignment is a randomized comparison when the instrument is randomized, but it is not by itself the treatment effect when uptake differs. An instrumental-variable analysis adds exclusion and monotonicity to interpret the change in outcomes through the change in treatment. Matching or covariate adjustment may address measured differences in nonrandomized settings, but neither automatically establishes exclusion or removes unmeasured confounding of the instrument.
The LATE is local in the sense that it applies to compliers in the population and setting where the instrument operates. Another encouragement, treatment-access policy, or population can produce a different complier group and a different average effect. The result does not by itself identify the average treatment effect for everyone or for those who actually received treatment.
A common mistake is to say, “The encouragement was randomized, so the instrumental-variable estimate is causal.” Randomization supports independence, but it does not guarantee relevance, exclusion, or monotonicity. The correction is to assess each condition separately and then state the target population that the complete set of assumptions supports. An estimate may be precise and still fail to have the intended causal interpretation if one essential condition is implausible.
Check Your Understanding
Answer each question, then compare with the brief solutions below.
- If encouragement changes the treatment rate but also provides a service that directly changes the outcome, which assumption is in doubt?
- Why does a randomized encouragement not, by itself, identify the treatment effect for everyone?
- Suppose the outcome contrast is 2 points and the treatment contrast is 0.25. Under the joint assumptions, what is the identified effect and its target population?
- What does a small treatment-rate difference across instrument groups suggest, and which assumption does it concern?
- Why can defiers prevent the instrument contrast from identifying the complier effect alone?
Solutions. (1) Exclusion is in doubt because the encouragement has a route to the outcome other than treatment receipt. (2) Randomization supports independence, but relevance, exclusion, and monotonicity are also needed; moreover, the resulting target is generally compliers, not everyone. (3) \(2/0.25=8\) outcome units, as an average treatment effect among compliers, assuming the conditions hold. (4) It suggests weak relevance: encouragement may not shift treatment receipt enough for a stable ratio. (5) Defiers change treatment in the opposite direction from compliers, so their treatment and outcome changes enter the contrasts with the opposite sign.