Three Variables, Three Different Roles
In many studies, people who receive a treatment differ from those who do not. They may have different health, resources, preferences, or risks before treatment begins. A direct comparison of treated and untreated outcomes can therefore mix the effect of treatment with pre-existing differences. Instrumental-variable reasoning starts from a different question: is there some other variable that shifts who receives treatment, without itself creating the outcome differences we want to attribute to treatment?
The three variables must be kept distinct. Let \(Z\) denote the instrument, the source of variation used to learn about treatment. Let \(D\) denote the treatment actually received, and let \(Y\) denote the outcome. In a binary-treatment setting, \(D=1\) indicates receipt and \(D=0\) indicates nonreceipt. The instrument may be an encouragement, an offer, an assignment rule, or another feature that changes the chance of receiving treatment. It is not necessarily the treatment itself.
For example, a randomized invitation to a program can be an instrument for participation. The invitation \(Z\) is assigned, but some invited people decline and some uninvited people participate. Thus \(Z\) is randomized while \(D\) is not. Comparing people by \(D\) would discard the protection of random assignment; comparing them by \(Z\) preserves it. The instrument’s value is that it can create a treatment contrast among groups whose instrument values are not systematically tied to the outcome’s other causes.
How Instrument-Induced Variation Can Inform a Treatment Effect
A useful way to see the logic is to begin with a simple model. Suppose the outcome follows \(Y=\alpha+\tau D+\varepsilon\), where \(\alpha\) is a baseline level, \(\tau\) is a common causal effect of treatment, and \(\varepsilon\) collects other outcome causes. This model assumes a constant effect \(\tau\) for the population under study. Suppose also that changing \(Z\) does not directly change \(Y\), and that the instrument is unrelated to \(\varepsilon\). Finally, \(Z\) must actually shift treatment receipt.
For two instrument values, subtract the conditional mean at \(Z=0\) from the one at \(Z=1\). If \(E(\varepsilon\mid Z=1)=E(\varepsilon\mid Z=0)\), the error component cancels:
This is the central intuition: the instrument creates a difference in treatment receipt, and—under the model and assumptions—the corresponding outcome difference is attributable to that treatment variation. If the instrument does not change treatment receipt, it supplies no such leverage. If it changes the outcome through another route, or is related to other causes of the outcome, the cancellation argument fails.
This argument also clarifies what is and is not randomized. The instrument may be randomized, while treatment receipt remains self-selected. The treatment contrast induced by \(Z\) is useful precisely because it is generated by the instrument rather than by directly comparing everyone who chose treatment with everyone who did not. The assumptions concern the source and pathways of instrument variation; they do not assert that all treated people are comparable to all untreated people.
Worked Example: A Randomized Program Invitation
Hypothetical data. A study randomly assigns 200 people to receive either an invitation to a support program or no invitation, with 100 people in each group. Participation is the treatment \(D\). At follow-up, the outcome \(Y\) is a well-being score from 0 to 20, with higher scores indicating better well-being. Among invited people, 60 participate and the total of their group’s outcome scores is 1,300. Among those not invited, 30 participate and the outcome-score total is 1,050.
The treatment rates are \(60/100=0.60\) in the invited group and \(30/100=0.30\) in the uninvited group. Thus invitation changes the observed participation rate by \(0.60-0.30=0.30\), or 30 percentage points.
The outcome means are \(1{,}300/100=13.0\) points for the invited group and \(1{,}050/100=10.5\) points for the uninvited group. Their difference is \(13.0-10.5=2.5\) points. Because invitation was randomized, this contrast estimates the effect of being invited, subject to ordinary concerns such as missing outcomes and chance variation.
The 2.5-point contrast is not automatically the causal effect of participation. Some invited people did not participate, and some uninvited people did. To use invitation to learn about participation’s effect, the study must also support the claim that invitation has no outcome pathway other than its effect on participation. For instance, if the invitation itself provides useful information that improves well-being even without participation, that claim is doubtful. The calculation shows an instrument-induced treatment difference and an instrument-associated outcome difference; the assumptions determine whether the latter can be attributed to treatment.
What Must Be Believed About the Instrument
Three requirements summarize the causal argument. They are not interchangeable, and evidence for one does not establish the others.
- Relevance: \(Z\) must change the distribution of \(D\). If the instrument never alters treatment receipt, it cannot generate a treatment contrast. A strong-looking association is useful for this requirement, but says nothing by itself about the other two.
- Independence: the instrument must be independent of the outcome’s other causes, either by design or by a defensible argument about how \(Z\) was generated. Random assignment is one possible basis. In an observational setting, an instrument might instead be entangled with geography, access, or socioeconomic conditions that also affect \(Y\).
- Exclusion: the instrument must affect the outcome only through treatment receipt. An invitation that changes motivation or access to other services may influence \(Y\) directly, even if it also changes \(D\).
In the simple model above, independence makes the average error component the same across instrument values, and exclusion is represented by the absence of a direct \(Z\) term in the outcome equation. These are substantive causal claims, not routine properties of a variable. They should be argued from the study design and subject-matter knowledge. A statistical association between \(Z\) and \(D\) can be examined in data, but the absence of a direct pathway from \(Z\) to \(Y\) is generally not established just by inspecting those data.
Worked Example: Physician Preference as a Candidate Instrument
Hypothetical data. Suppose patients are treated by physicians with either a high or low historical preference for prescribing a medication. In each group of 100 patients, 72 patients of high-preference physicians receive the medication, compared with 48 patients of low-preference physicians. Average recovery time is 7.8 days in the high-preference group and 7.1 days in the low-preference group.
The treatment-rate contrast is \(72/100-48/100=0.24\), or 24 percentage points. The mean recovery-time contrast, defined as high preference minus low preference, is \(7.8-7.1=0.7\) days. Since shorter recovery is better, the high-preference group has a 0.7-day longer average recovery time.
The treatment-rate difference makes physician preference a candidate source of treatment variation. It does not show that preference is a valid instrument. High-preference physicians might work in hospitals with different recovery practices, or might treat patients with different underlying risks. Either possibility can associate preference with outcome causes, challenging independence. A physician’s preference could also affect other aspects of care, challenging exclusion. The arithmetic establishes the observed contrasts; deciding whether they support a causal treatment conclusion requires a design-based argument for the assumptions.
Instrument Effects Are Not Treatment Effects
An instrument’s effect on an outcome is often called an assignment or reduced-form effect: it compares outcomes across values of \(Z\). It answers a question about changing the instrument, such as offering a program or changing eligibility. The treatment effect asks what would happen to outcomes if treatment receipt \(D\) itself were changed. Those are different causal questions.
If everyone complied perfectly with a randomized treatment assignment, the distinction might be less visible. With noncompliance, the instrument changes treatment for only some people, and some treatment may occur even without the instrument. The outcome contrast by \(Z\) therefore reflects the instrument’s effect on the population, not automatically the effect of treatment for every person. Interpreting it as evidence about treatment requires a model and assumptions connecting the instrument-induced change in \(D\) to \(Y\).
Under the constant-effect model, the displayed equation makes that connection explicit: the outcome contrast equals the common treatment effect multiplied by the treatment-rate contrast. If effects vary across people, this simple model no longer says that the induced variation represents the population’s average treatment effect. The causal target can depend on whose treatment receipt the instrument changes and on additional assumptions. Thus “IV identifies the treatment effect” is incomplete unless the target population or effect and the identifying conditions are specified.
Worked Example: A Policy That Also Changes School Resources
Hypothetical data. Two groups of 100 students are compared. A district policy makes tutoring more available in one group: 65 students receive tutoring there, compared with 40 students in the other group. Average test scores are 78 and 74 points, respectively.
The tutoring-rate contrast is \(65/100-40/100=0.25\), or 25 percentage points. The score contrast is \(78-74=4\) points. If the policy were unrelated to other causes of scores and affected scores only by changing tutoring, these contrasts could provide an instrument-based route to studying tutoring’s effect.
Now suppose the policy group also receives new classroom materials that directly improve test scores. That creates a path from policy status to the outcome that does not run through tutoring, violating exclusion. Alternatively, if the policy was introduced first in schools with unusually strong prior achievement, independence may fail. In either case, the 25-percentage-point and 4-point contrasts remain arithmetically correct, but they do not isolate tutoring’s causal effect. This example illustrates why a policy can strongly predict treatment and still be a poor instrument.
A Practical Assessment Before Using an Instrument
Before interpreting an IV analysis, describe the proposed source of variation in ordinary language. Specify what \(Z\) is, how it is generated, how it changes \(D\), and which routes from \(Z\) to \(Y\) might bypass treatment. Then distinguish the observed evidence from the assumptions:
State the instrument \(Z\), the treatment received \(D\), and the outcome \(Y\). Make clear which one is assigned or otherwise varies exogenously and which one is actually received.
Compare treatment receipt across instrument values. A negligible shift means the instrument supplies little treatment variation, even if its proposed design sounds persuasive.
Explain why instrument values are not tied to other outcome causes and why the instrument has no outcome pathway outside treatment. Do not treat these claims as established merely because \(Z\) predicts \(D\).
Separate the effect of changing \(Z\) from the effect of changing \(D\). Say what additional model or assumptions connect the two, and avoid claiming a population-wide treatment effect when the design does not support it.
Common Mistake: Treating an Instrument Like Randomized Treatment
A frequent error is to see that \(Z\) was randomized, compare outcomes by \(Z\), and report that difference as the treatment effect. The comparison is generally an effect of the instrument, such as an offer or encouragement. It equals a treatment effect only under further conditions that connect the instrument’s effect on \(Y\) to its effect on \(D\). A related error is to see a strong \(Z\)-to-\(D\) association and conclude that the instrument is valid. That supports relevance, not independence or exclusion.
Check Your Understanding
For each question, separate the observed contrast from the causal claim it might support.
- A randomized reminder increases medication use. Name \(Z\), \(D\), and \(Y\) in a proposed study, and explain why the reminder’s outcome contrast is not automatically the medication effect.
- In the simple model \(Y=\alpha+\tau D+\varepsilon\), what happens to the outcome contrast across instrument values if the instrument shifts treatment but the mean of \(\varepsilon\) is the same in both groups?
- A proposed instrument strongly predicts treatment but is also associated with patients’ baseline disease severity. Which requirement is in doubt, and why does treatment prediction not resolve that concern?
- A policy increases participation and supplies additional services that can affect the outcome directly. Which IV requirement is threatened?
- Explain the difference between an effect of an instrument on an outcome and a causal effect of treatment on that outcome.