Department of Epidemiology, UCLA School of Public Health, Los Angeles, CA 90095-1772, USA.
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Abstract |
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Keywords Biometry, causal models, compliance, confounding, econometrics, epidemiological methods, instrumental variables, measurement error, misclassification, regression, regression calibration, statistics
Accepted 17 December 1999
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Introduction |
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An intuitive basis for the methods discussed here is as follows: Suppose X and Y are the exposure and outcome of interest, and we can observe their relation to a third variable Z, called an instrumental variable or instrument, that is associated with X but not associated with Y except through its association with X. Then, under certain conditions, we can write the Z-Y association as a product of the Z-X and X-Y associations,
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Instrumental variables for confounding control |
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Note that assumption 3 implies that Z has no direct effect on Y. Figure 1 gives a causal diagram17 that satisfies these assumptions, with labels from the example below.
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Intrumental variable methods for non-compliance |
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Confounding is a threat whenever people fail to comply with their assignment (i.e. have X Z) for reasons (U) related to their outcome;410,18,19,22,23 this problem is often referred to as one of biased selection for treatment. For example, patients assigned to a complex pill regimen may become lax in following that regimen. These non-compliers are often those who feel less ill and who have a better prognosis with respect to the outcome Y. In such situations, there will be confounding in a comparison of those complying with treatment to the other patients, because those complying are sicker than the others (i.e. there is self-selection for treatment that is related to prognosis).
Concerns of this sort have led to recommendations (often rigid) that intent-to-treat analysis be followed. To test and estimate effects, intent-to-treat compares those assigned to one treatment against those assigned to another treatment without regard to actual treatment received (X). Critics of this approach point out that treatment received is the source of biological efficacy, and that comparison of treatment assigned is biased for the effect of treatment received (furthermore, the bias is not always toward the null,24 contrary to common lore). By recognizing treatment assignment as an instrument, IV methods provide an alternative to the biased extremes of analysing Z as the treatment (intent-to-treat) and analysing received treatment X in the conventional manner (which is likely to be confounded by determinants of compliance).
To see how the IV concept can be used to control for confounding due to non-compliance, let us refer to people who would always obey their treatment assignment as co-operative; among these people, X and Z are always equal. It is crucial to distinguish the concept of co-operative people from the concept of compliance. Co-operative people are those who will receive their assigned regimen, no matter which regimen (treatment) they are assigned. In the example, co-operative children have parents or guardians who will fully co-operate with the researchers, in that they will allow the researchers to give their child the vitamin if assigned to receive it, and will not give their child the vitamin if assigned to not receive it. Non-co-operative people are those who will not receive certain regimens if assigned to them. In the example, some parents may refuse to let their child receive the experimental treatment. These refusers have children who exhibit non-compliance if they are assigned to the vitamin A, but who exhibit compliance if they are assigned to no vitamin. Thus, some non-co-operative people will be in compliance with their assignment, simply because they were not assigned to a treatment they would have refused.
Following earlier derivations of the correction below,8,19 I will introduce this simplifying assumption:
4) Treatment assignment affects X only among co-operative people.
This assumption says that the participants may be divided into two groups: co-operative, for whom X always equals Z; and non-co-operative, for whom assignment Z has no effect on X. If the treatment variable has only two levels (1 and 0), assumption 4 reduces to an assumption that no trial participant would always (perversely) receive the opposite of what she was assigned, no matter which treatment she was assigned,8 so that there are only two types of non-co-operators: Those who would always receive treatment and those who would never receive treatment. Table 1 provides evidence that assumption 4 is satisfied in the example: If there were participants who would always receive the opposite of their assignment ( defiers8), we should expect to see some of them in the Z = 0, X = 1 column, but no one is seen there.
Now define
pc = proportion of trial participants who are co-operative.
pc is the effect that assignment to treatment 1 rather than 0 would have on the average value of the treatment indicator X. To see this, define
p1 = proportion of participants who would receive treatment 1 (X = 1) if assigned treatment 1 (Z = 1)
= average of X if everyone were assigned treatment 1
p0 = proportion of participants who would receive treatment 1 (X = 1) if assigned treatment 0 (Z = 0)
= average of X if no one were assigned treatment 1.
Any difference between p1 and p0 has to be due to the change in X among co-operative people (because, by assumption 4, only the co-operative people are affected by Z). More precisely, p1 p0 must equal pc because only co-operative people would go from X = 0 to X = 1 in response to a change from Z = 0 to Z = 1. Also, p0 must equal the proportion of nonco-operators who always receive treatment, 1p1 must equal the proportion of non-co-operators who never receive treatment, and pc + p0 + 1 p1 = 1.
Under assumption 1, p1 p0 and hence pc is validly estimated by the observed difference in the proportion receiving treatment 1 (X = 1) for the group assigned treatment 1 (Z = 1) versus the group assigned treatment 0 (Z = 0). In the example, this estimate is the difference in the proportions receiving vitamin A among those assigned and not assigned to A:
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Next, define
m1= average outcome () if everyone is assigned treatment 1 (Z = 1)
m0= average outcome if everyone is assigned treatment 0 (Z = 0).
The average outcome difference m1 m0 is the effect that assignment to treatment 1 rather than 0 would have on the average outcome. (Recall that, when Y is a binary (0,1) disease indicator, the average outcome is the average risk or incidence proportion, and the average outcome difference is the average risk difference.25) Under assumption 1, this difference is validly estimated by the observed difference in average outcome for the group assigned treatment 1 versus the group assigned treatment 0 (which is the intent-to-treat [ITT] estimate of treatment effect):
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Next, consider two quantities that we do not observe directly:
m1c = average outcome of co-operative people if everyone is assigned treatment 1,
m0c = average outcome of co-operative people if everyone is assigned treatment 0.
m1c m0c is the effect that assignment to treatment 1 rather than 0 would have on the average outcome of co-operative people. In addition, because assignment Z and treatment received X are identical among co-operative people, m1c m0c is the effect that receiving treatment 1 rather than 0 would have on the average outcome among co-operative people. In other words, m1c m0c is both an intent-to-treat (Z) effect and a biological (X) effect on co-operative people.
Finally, consider two quantities that are estimable in a randomized trial:
m1n = average outcome among non-co-operative people who receive treatment
m0n = average outcome among non-co-operative people who do not receive treatment.
Under assumptions 3 and 4, these averages do not depend on assignment Z. Thus, m1n can be estimated directly from the average outcome of those assigned to 0 but receiving 1 (Z = 0, X = 1); similarly, m0n can be estimated directly from the average outcome of those assigned to 1 but receiving 0 (Z = 1, X = 0).
Table 2 summarizes the data expected from a study satisfying assumptions 14, using the above notation. It shows that we can write m1, the average outcome if everyone were assigned treatment 1, as a weighted average of the average outcomes for co-operative people and non-co-operative people, with weights equal to the respective proportions of each type of person:
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We can solve equation 3 for the effect of treatment X among co-operative people to get
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This equation shows that, subject to the assumptions, we can estimate the effect of treatment received X on the average outcome among co-operative people as the estimated effect of treatment assignment Z on the overall average outcome divided by the estimated effect of treatment assignment on the received treatment X. The Appendix gives a formula for the variance of this estimate. Because m1 m0 and p1 p0 equal the Z-coefficients from the linear regressions of Y on Z and X on Z, the effect estimate from equation 4 equals the classical IV-regression estimate.2
Returning to the example, the unadjusted estimate of the risk difference produced by treatment (which is confounded by non-compliance) compares X = 1 to X = 0:
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Choice of target effect
In the above example the effect of vitamin A, m1c m0c, is an effect restricted to co-operative people. This effect is useful if we think that co-operative people in the trial are typical (with respect to treatment effect) of people who will accept the treatment they are assigned. Aside from such generalizability issues (which arise in all trials), a conceptual problem is that we often cannot identify co-operative people with any certainty.8,18 We can of course ask trial participants (or, above, their parents) assigned to and receiving a treatment if they would have obtained and taken that treatment had they not been assigned to it, but the reliability of the responses would ordinarily be unknown (even to the participant).
Under assumption 4 and the assumption that the treatment would never be received by those not assigned to it (which is plausible in the above example), we may identify as co-operative those people who receive treatment among those assigned to treatment. Otherwise, although we can estimate the proportion pc of co-operative people (to whom our estimate of m1c m0c applies), we cannot characterize those people. The only behavioural effect we can always identify is the effect of assignment Z on treatment received X within our trial.
Sometimes, the effects of treatment under strictly enforced regimens are of central interest in planning mandatory programmes of otherwise unavailable prophylactics (such as vaccines). Define
mjf = average outcome if everyone were forced to receive treatment j.
In the example, m1f m0f is the effect of forcing every child to take vitamin A versus withholding the supplement from every child. If co-operative and non-co-operative people differ in any way related to the effect of treatment received (i.e. if the variable co-operative/non-co-operative modifies the effect of X), the effect of X among co-operative people will not suffice to estimate the forcing effect. Unfortunately, we should expect the selective non-compliance that confounds the naïve X = 1 versus X = 0 comparison to also make m1c m0c unequal to m1f m0f. Thus, one should never presume that the IV estimate of the effect is a valid estimate of the forcing effect, even when it is a valid estimate of the effect on co-operative people.
Estimation of ratio measures
A problem arises if one wishes to estimate measures that are ratios of average outcomes, reflective of more general non-collapsibility problems of ratio measures:25,26 Because logs of averages are not averages of logs, one cannot simply take Y as (say) the log rate or log odds and apply the above formulas to differences in these logs to obtain corrected log relative risk estimates; one needs additional strong assumptions about homogeneity of risks within levels of X and all controlled covariates to use the formulas. Such assumptions are implicit in IV methods based on regression modelling.2,1116
Alternatively, under assumptions 13 and one more assumption one may derive risk ratio (RR) estimators for the effect of treatment among co-operative people, as well as alternative risk-difference (RD) estimators18,23 (note, however, that the formulas in Sommer and Zeger18 have serious misprints). For example, suppose that p0 = 0, i.e. one cannot get treatment 1 (X = 1) without assignment to treatment 1 (Z = 1), so that the only non-co-operators are those who do not receive treatment when assigned to treatment (as in the example). Then, from assumptions 1 and 3,
The proportion receiving treatment among the proportion assigned to treatment, 1, is a valid estimate of pc.
People assigned to and receiving treatment (Z = X = 1) are representative of all co-operative people in the trial, and so their average outcome provides a valid estimate of m1c; call it 1c.
People assigned to but not receiving treatment (Z = 1, X = 0) are representative of non-co-operative people in the trial, and so their average outcome provides a valid estimate of m0n; call it 0n.
As before, we can also estimate m0 by the average outcome among those assigned to 0 (Z = 0), 0.
We can now solve equation 2 for m0c to obtain
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The latter estimate is the same as the estimate obtained from equation 4, although it was derived from the assumption that p0 = 0, which is stronger than assumption 4 (from which equation 4
was derived).
Cuzick et al.23 derived a more general risk-ratio estimator under an alternative assumption that the ratio is the same (homogeneous) for co-operators and for all types of non-compliers; when 1 = 0 (as in the example), their estimator reduces to that just given. As with the other estimators, their estimator also requires assumptions 13. Connor et al.27 also derived formula 5 in the context in which treatment is screening and compliance is acceptance of screening, using assumptions equivalent to 13 and p0 = 0.
Insufficiency of the instrumental assumptions
Assumptions 13, which here define Z as an instrument, are not sufficient to yield a point estimate of effects of the received treatment X. They do allow setting of bounds for X effects,4,6,7,10 but these bounds can be uselessly wide.9 Using only assumptions 13 in the above example, Balke and Pearl10 derived non-parametric bounds for the forcing risk difference m1f m0f of 0.5% and 19%. The details of their derivation are beyond the present paper, but their upper bound suggests vitamin A might kill up to a fifth of the children, an absurd value in light of the extensive background information on the non-toxicity of vitamin A in the doses administered.20 Thus, assumptions 13 plus the example data provide almost no additional information beyond what is already known to place an upper bound on the risk difference.
To obtain useful results, one will often need further plausible biological (causal) or parametric statistical assumptions beyond those embodied in assumptions 13. In the above example, assumption 4 is quite plausible. An even more plausible assumption is that vitamin A would not kill any of the children. With this no harm assumption replacing assumption 4, the ITT estimate (-0.26%) is an upper bound for the forcing risk difference; this bound is obtained by assuming that no death in the group with Z = 1 and X = 0 (who are non-co-operative people) would have been prevented by forcing every child to take vitamin A. A companion lower bound of 12/12 094 74/11 584 = 0.54% is obtained by assuming that every death in the group with Z = 1 and X = 0 would have been prevented by forcing treatment on these children. These bounds are only for the point estimate of effect that would be obtained under a forced regimen; they do not account for random errors in the numbers of deaths. Nonetheless, the lower bound is already implausibly low on biological grounds, for we can be sure that treatment could not have prevented every death in the Z = 1, X = 0 group.
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Instrumental variables for misclassification correction |
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3') Z is independent of Y given X
This assumption corresponds to the notion that error in Z as a measure of X is non-differential with respect to the outcome; this error may have systematic as well as random components, as long as neither component is associated with Y.
Given assumptions 2 and 3', we can validly estimate the association of Y with X using IV formulas, provided we have validation data that show how Z predicts X in our study (i.e. that provide estimates of the predictive values for Z as a measure of X). To see this relation for a binary exposure X in a cohort study, for each exposure level j (j = 1 or 0) define
mX=j= average outcome among those with X = j
mZ=j= average outcome among those with Z = j
pj = probability that X = 1 when Z = j for the entire cohort;
p1 and 1 p0 are then the positive and negative predictive values for the entire cohort (without regard to the outcome).
Under assumption 3', Z has no effect on Y other than through Z; hence, the average outcomes within levels of X do not change across levels of Z, and in particular equal the mX=j. Furthermore, the average outcome mZ=j within a given level j of Z is just the average of the average outcomes within levels of X, weighted by the probabilities of the X levels within the Z level; that is,
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This equation shows that, subject to the assumptions, we can estimate the exposure-specific outcome difference as the ratio of the surrogate-specific outcome difference (the Z-Y association) and the difference of the surrogate-specific probabilities of X = 1 (the Z-X association).
Use of validation data
Equation 8 does not require any data that directly relate the true exposure X to the outcome Y: We can correct the estimate from a study relating the surrogate Z to the outcome provided we can construct accurate estimates of p1 and p0 from a validation study relating the true exposure to the surrogate. If, however, the validation data also show the relation of the true exposure to the outcome (as would be the case if they were a random sample from the study relating surrogate to outcome), the IV-corrected estimate from applying equation 8
to the unvalidated data can and should be combined with the direct estimate from the validation data. Such data combination is done most efficiently with regression modelling.15,28 Validation data that are not restricted on the outcome (e.g. that include both cases and non-cases when Y is a disease indicator) also allow one to test assumption 3 and to use methods that do not require that assumption.2830
Relation to confounding control
The resemblance of equation 8 to 4
reflects an underlying common feature of the two situations. In both, we lack complete data on the relation of X to Y. In the non-compliance problem, we lack data on who is co-operative; the IV method uses the X-Z data to correct for the dilution of the Z-Y association as a measure of the X effect that results from inclusion of non- co-operative people in the intent-to-treat comparison. Similarly, in the classification problem we lack data on who is correctly classified; the IV method uses X-Z data to correct for the dilution resulting from the inclusion of the misclassified data in our comparison.
There is a distinction, however: For misclassification, assumption 3' implies that the X-Y association is the same among the correctly and incorrectly classified; hence, the corrected estimate applies to the entire study cohort. In contrast, for confounding control, the assumptions do not imply that the effect of X on Y would be the same for co-operative and nonco-operative people; hence, the corrected estimate applies only to co-operative people (who may be difficult to identify). This distinction does not appear in classical IV methods, as these methods are based on models in which the X effect on Y is homogeneous across covariates U. (Note that, by assumption 3, Z has no effect and so the X effect must be homogeneous within levels of Z.)
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Discussion |
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An important limitation of corrections based on regression models is their model dependence, especially on the models for error distributions. For example, P-values and confidence limits from the basic regression-calibration (linear-imputation) form of IV correction assumes that the regression of the true (biologically relevant) exposure X on the instrument Z follows a linear model with normal errors.13,29 This model is highly implausible in many situations and is mechanically impossible to satisfy if X and Z are discrete. This limitation is not shared by non-parametric methods410 and special methods for categorical variables.3032
In purely observational studies (in which neither the instrument Z nor the treatment X has been subject to experimental manipulation), a major limitation of all IV methods is their strong dependence on assumptions 1 and 3. The corrections may even be harmful if Z is associated with other errors or with unmeasured confounders, as might be expected if (say) Z is self-reported alcohol consumption, X is true consumption, Y is cognitive function, and U is use of illegal drugs. Thus, IV corrections are no cure for differential errors; they address only independent non-differential errors, as embodied by assumptions 1 and 3. If there are violations of the assumptions, bias due to measurement error (using Z as a surrogate for X) will no longer act multiplicatively (as in formula 7) and adjustment will require more complex formulas.15,28
The sensitivity of IV corrections to the assumptions increases with the amount of non-compliance or the amount of error in Z as a measure of X; the corrections will be especially unreliable if Z is a very noisy measure of X, so that the association of Z and X is weak.33 The key to successful IV correction is thus to find an instrument Z that is strongly associated with the exposure X but not otherwise associated with uncontrolled factors affecting Y or with other sources of error. Such instruments may be difficult to find when only self reports of sensitive personal characteristics are available, but can sometimes be found or created from records or physical measurements.13,15
Finally, one should be aware that the IV corrections (like most epidemiological statistics) are large-sample procedures, which means they include some bias due to sample-size limitations, even if all the assumptions are met. For linear-regression IV corrections this bias is in the direction of undercorrection,33 and so should be of less concern than the effects of biased measurement. Furthermore, this bias decreases with increasing association between Z and X,33 which provides further impetus to find instruments highly associated with X.
Despite the aforementioned cautions, IV corrections can be valuable in many situations. When the IV assumptions are questionable, the corrections can still serve as part of sensitivity analysis or external adjustment.34 When the assumptions are more defensible, as in field trials and in studies that obtain validation or reliability data, IV methods can form an integral part of the analysis.
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Appendix |
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Let d be the IV parameter (m1 m0)/pc and the IV estimator (
1
0)/
c. Combining A1A4 with the Taylor approximation for variances of ratios of random variables35 yields
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An estimate of var() is obtained by substituting sample estimates for parameters in A5.
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Acknowledgments |
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References |
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