Why Instrument Assignment Must Be Independent
An instrument is useful because it changes treatment receipt in a way that can reveal a causal effect. But a strong association between an instrument and treatment is not enough. The instrument must also be independent of the potential outcomes and treatment responses that would have occurred under each instrument value. When assignment is selective, the instrument may separate people who would have had different outcomes even without treatment, or people with different propensities to comply.
This tutorial focuses on threats to that independence condition. It sets aside other requirements for LATE identification, such as exclusion and monotonicity, except where they are needed to isolate the effect of nonindependent assignment. An observed imbalance can flag a problem, but the central concern is deeper: whether instrument status is associated with unobserved potential outcomes or compliance behavior.
The joint condition matters. Independence from outcome potential outcomes alone is not enough if instrument status sorts people by their potential treatment responses. Those responses determine who would be a complier, always-taker, never-taker, or defier. If assignment favors people who are more likely to comply, the instrument can select a different mix of compliance types.
Conditional independence can be plausible when assignment is not random overall but is as-if random after accounting for measured baseline covariates. It also requires overlap: within the covariate strata used for adjustment, there must be a positive chance of either instrument value. If a stratum contains only instrumented or only uninstrumented individuals, its counterfactual instrument contrast cannot be learned from that stratum’s data.
How Selection Enters the Wald Contrast
Suppose, for the moment, that exclusion holds, so the instrument affects the outcome only through treatment, and that treatment is binary. Then the observed outcome under instrument value \(z\) is \(Y_i(D_i(z))\). Without independence, the groups defined by \(Z=1\) and \(Z=0\) need not represent the same distribution of potential outcomes or potential treatment responses.
A useful decomposition shows the issue. Write \(\tau_i=Y_i(1)-Y_i(0)\). Under exclusion, \(Y_i(D_i(z))=Y_i(0)+\tau_iD_i(z)\). Therefore the observed reduced-form contrast is
The first line is a difference in untreated potential outcomes between instrument groups. It is a selection contrast, not a treatment effect. The second line also compares treatment responses among groups that may differ in both treatment gains and compliance. The observed first stage, \(E[D\mid Z=1]-E[D\mid Z=0]\), is likewise not necessarily the population average \(E[D(1)-D(0)]\) when instrument status is selected.
Under independence, the groups have the same distribution of the potential quantities. If monotonicity also holds, the outcome contrast is \(P(C)\,E[Y(1)-Y(0)\mid C]\), where \(C\) denotes the complier type, and the first stage is \(P(C)\). Their ratio is the LATE. This is the key justification for the Wald interpretation; selection can break the equalities before the ratio is formed.
Worked Example: Selective Encouragement by Prognosis
Consider a hypothetical program in which \(Z=1\) means receiving an encouragement to start treatment. High-prognosis individuals are more likely to be encouraged: 80% of those with high baseline prognosis receive encouragement, compared with 20% of those with low prognosis. Suppose half the population has each prognosis level. Everyone takes treatment if encouraged and no one takes it otherwise, so \(D_i(1)=1\) and \(D_i(0)=0\) for all individuals. Let untreated outcomes be 10 for high-prognosis individuals and 0 for low-prognosis individuals; treatment adds 2 outcome units for everyone.
Because the prognosis groups are equally prevalent, the fraction high-prognosis among the encouraged is 0.80, and among the unencouraged it is 0.20. The observed mean outcome for the encouraged group is \(0.80(10+2)+0.20(0+2)=10.0\). For the unencouraged group it is \(0.20(10)+0.80(0)=2.0\). The outcome contrast is \(10.0-2.0=8.0\) units. The treatment contrast is \(1-0=1\), so the Wald ratio is \(8.0/1=8.0\) outcome units per treatment.
The true treatment effect for every individual, and therefore the true LATE among the all-complier population, is 2 outcome units. The discrepancy arises because encouragement is associated with prognosis: the untreated-outcome contrast is \(0.80(10)+0.20(0)-[0.20(10)+0.80(0)]=6.0\) units. Adding that selection contrast to the 2-unit treatment effect produces the 8-unit reduced form. Even perfect compliance and a nonzero first stage do not protect the Wald ratio from selective assignment.
Common Assignment Mechanisms That Threaten Independence
Selective encouragement occurs when staff, clinicians, or participants decide who receives an offer or reminder based on expected benefit, illness severity, motivation, or anticipated adherence. Those features can predict \(Y_i(0)\) or \(Y_i(1)\), and can also predict \(D_i(0)\) or \(D_i(1)\). A protocol described as an encouragement design is not automatically randomized; the actual process that determines who is encouraged is what matters.
Nonrandom eligibility arises when instrument status is defined by a rule or status related to prognosis. Eligibility based on clinical severity, employment, or a demographic threshold may differ systematically from random assignment. A threshold rule can sometimes support a local design under additional conditions, but merely labeling eligibility as an instrument does not make it independent. The relevant question is whether potential outcomes and potential treatment responses are comparable across instrument values in the analysis population, perhaps conditional on appropriate baseline covariates.
Worked Example: Eligibility Based on Clinical Severity
In a hypothetical service program, eligibility \(Z=1\) is more common for patients with severe baseline symptoms. Suppose 75% of eligible patients are severe, compared with 25% of ineligible patients. Everyone eligible receives treatment and no one ineligible does. Untreated outcomes average 20 points for severe patients and 5 points for less-severe patients; treatment improves the outcome by 3 points for each patient.
The eligible group’s mean outcome is \(0.75(20+3)+0.25(5+3)=19.25\) points. The ineligible group’s mean is \(0.25(20)+0.75(5)=8.75\) points. The first stage is \(1-0=1\), so the observed Wald ratio is \((19.25-8.75)/1=10.5\) points per treatment.
The treatment effect is 3 points for everyone, so 10.5 is not the causal effect. The untreated-outcome contrast alone is \([0.75(20)+0.25(5)]-[0.25(20)+0.75(5)]=7.5\) points. Thus the 10.5-point reduced form combines a 7.5-point severity-composition difference and a 3-point treatment effect. Measuring severity could address this particular selection pathway only if conditioning on severity makes instrument assignment independent of the remaining potential outcomes and treatment responses, and if both eligibility states occur at each severity level. Those are substantive conditions, not consequences of including a covariate in a model.
Differential access can threaten independence even when the instrument is nominally assigned by a common rule. Instrument status may be more common in locations with easier treatment access, while access also predicts baseline outcomes. Access can also change who responds to an offer, associating \(Z\) with the distribution of compliance types. This second pathway matters even if baseline outcomes happen to be similar: a LATE is an effect for compliers, and selective assignment can change which people are represented among those compliers.
Worked Example: Differential Access Changes the Wald Ratio
Suppose a hypothetical population is evenly divided between high-access and low-access areas. The instrument is more common in high-access areas: \(P(Z=1\mid A=\text{high})=0.80\) and \(P(Z=1\mid A=\text{low})=0.20\). Within each access area, half the people are compliers and half are never-takers; there are no always-takers or defiers. Treatment effects are 1 outcome unit in the high-access area and 5 units in the low-access area. Untreated outcomes are 10 units in the high-access area and 0 in the low-access area. Assume assignment is otherwise independent within each area and exclusion holds.
The equal area sizes imply that 80% of the \(Z=1\) group is high-access and 20% is low-access; the \(Z=0\) group has the reverse proportions. Among \(Z=1\), half receive treatment in each area, so the mean outcome is \(0.80[10+0.50(1)]+0.20[0+0.50(5)]=8.9\). No \(Z=0\) individual receives treatment, giving a mean outcome of \(0.20(10)+0.80(0)=2.0\). The reduced form is \(8.9-2.0=6.9\) units, and the first stage is \(0.50-0=0.50\). The pooled Wald ratio is \(6.9/0.50=13.8\) units per treatment.
The complier effect in the high-access area is 1 unit, and in the low-access area it is 5 units. Since each area contributes the same number of compliers, the LATE among all compliers is \((1+5)/2=3\) units. The pooled ratio of 13.8 instead includes a 6-unit untreated-outcome composition contrast, divided by the 0.50 first stage, as well as the treatment-effect contribution. An analysis that conditions on access can remove this measured composition difference if the within-area assumptions hold; it must still define how area-specific complier effects are combined for the target population.
Diagnostics, Adjustment, and Limits
A credible independence argument starts with the assignment mechanism, not a statistical test. Document who chose or determined \(Z\), when it was determined, which eligibility and access rules applied, and whether those rules used prognostic information. Then examine pre-instrument covariates that could represent those mechanisms.
- Check baseline balance. Compare covariates measured before instrument assignment across \(Z\) groups, preferably within the covariate strata used for conditional analyses. Large imbalances can reveal selection; small differences do not establish independence from unmeasured potential outcomes.
- Check overlap. Inspect whether both instrument values occur across relevant covariate patterns. Sparse or empty strata make conditional contrasts unstable or unidentified.
- Check timing and measurement. A covariate measured after instrument assignment may itself be affected by \(Z\). Adjusting for it can introduce bias rather than repair baseline selection.
- Probe the proposed mechanism. Compare assignment rates across sites, clinicians, severity groups, and access measures that plausibly influenced instrument status. Placebo outcomes or negative-control measures can expose some problems, but a reassuring result cannot verify independence for all potential outcomes.
When conditional independence is plausible given measured \(X\), estimate instrument-outcome and instrument-treatment contrasts within covariate strata and use a stated target distribution to combine them. This is different from simply adding covariates to a regression: adjustment works only if the chosen covariates suffice to make assignment independent and the needed overlap exists. Standard regression adjustment or propensity score matching is not a guarantee against unmeasured selection, nor does a good treatment-prediction model by itself establish instrument independence.
Random assignment of the instrument is the clearest design-based route to independence, subject to implementation and missing-data concerns. In observational settings, investigators instead rely on conditional independence arguments and measured adjustment. Neither balance tests nor fitted models can rule out every unmeasured factor related to potential outcomes or compliance. If important threats remain plausible, report that the LATE interpretation depends on an unverified assumption and consider sensitivity analyses or alternative designs rather than treating the Wald ratio as automatically causal.
Check Your Understanding
Answer each question, then compare your reasoning with the solutions.
- In one sentence, state the joint potential-outcome condition required for unconditional instrument independence.
- An encouragement is assigned more often to patients with severe disease. Name two distinct potential quantities that severity might be associated with.
- Suppose a measured covariate \(X\) is used to condition on assignment. What additional support condition is needed to estimate instrument contrasts within \(X\) strata?
- Why does balance on measured baseline covariates not prove instrument independence?
Solutions. (1) \(Z\) must be independent of the joint collection of \(Y_i(0),Y_i(1),D_i(0),D_i(1)\). (2) Severity could predict untreated or treated potential outcomes, such as \(Y_i(0)\), and could predict potential treatment receipt, such as \(D_i(1)\). Either association can threaten independence. (3) Both instrument values must have positive probability within the relevant \(X\) strata; otherwise the within-stratum contrast lacks support. (4) Balance concerns only measured covariates. Unmeasured causes of prognosis or compliance may still be associated with assignment, so observed balance cannot establish independence of the full potential-outcome and treatment-response collection.