the control of confounding by intermediate variables

STATISTICS IN MEDICINE, VOL. 8,679-701 (1989)

THE CONTROL OF CONFOUNDING BY INTERMEDIATE VARIABLES

JAMES ROBINS Occupational Health Program and Department of Biostatistics, Harvard School of Public Health,

Boston, M A 02115, U.S.A.

SUMMARY In epidemiologic studies of the effect of an exposure on disease, the crude association of exposure with disease may fail to reflect a causal association due to confounding by one or more covariates. Most previous discussions of confounding in the epidemiologic literature have considered only point exposure studies, that is, studies that measure exposure and covariate status only once, at start of follow-up. In this paper we offer definitions of confounding suitable for longitudinal studies that obtain data on exposure, covariate, and vital status at several points in time. An important difference between longitudinal studies and point exposure studies is that, in longitudinal studies, a time-dependent covariate can be simultaneously a confounder and an intermediate variable on the causal pathway from exposure to disease. In this paper I propose an estimator, the extended standardized risk difference, that provides control for confounding by a covariate that is simultaneously a confounder and an intermediate variable.

KEY WORDS Survival analysis Observational studies Longitudinal studies Causal inference Counterfactual causality

INTRODUCTION

In epidemiologic studies of the effect of an exposure on disease, the crude (i.e. marginal) association of exposure with disease may fail to reflect a causal association due to confounding by one or more covariates. This paper presents definitions of causal confounding suitable for longitudinal studies that obtain data on exposure, covariate, and vital status at several points in time.

An important difference between longitudinal studies and point exposure studies is that, in longitudinal studies, a time-dependent covariate Z can be simultaneously a confounder and an intermediate variable on the causal pathway from exposure to disease. Although estimators of the exposure effect that adjust for Z by stratification on covariate history may be unbiased for parameters that measure the magnitude of the direct effect of exposure on disease controlling for the intermediate variable 2, these estimators are biased for the parameter that measures the overall (i.e. total) effect of exposure on disease. This latter parameter is often the causal parameter of interest in epidemiologic research. Unfortunately, a ‘crude’ analysis that ignores the covariate can be biased for the overall exposure effect as well. In this paper, I propose an estimator, the extended standardized risk difference, that is an unbiased estimator of the overall effect of exposure even in the presence of a covariate that is simultaneously a confounder and an intermediate variable.

We will show that a time-dependent covariate Z may be a confounder for the overall effect of exposure if the covariate satisfies the following two conditions: for a subset of the population

0277-6715/89/060679-23li11.50 0 1989 by John Wiley & Sons, Ltd.

Received February 1988 Revised December 1988

680 JAMES ROBINS

disease free up to time t and matched on exposure history prior to t both (1) the disease rate at t depends on prior covariate history 2 (i.e. 2 is an independent risk factor for disease), and (2) the probability of exposure at t depends on Z-history through t (i.e. Z is a predictor of exposure).

In any observational study in which there is ‘treatment by indication’ there will exist risk factors for disease that are also predictors of exposure. For example, many physicians withdraw women from exogenous oestrogens at the time they develop an elevated blood cholesterol. Therefore, in a study of the effect of post-menopausal oestrogen on cardiac mortality, the cardiac risk factor cholesterol is a predictor of exposure. As a second example, in observational studies of the efficacy of cervical cancer screening on mortality, women who have had operative removal of their cervix due to invasive disease are no longer at risk for further screening (i.e. exposure) but are at increased risk for death. Therefore, the covariate ‘operative removal of the cervix’ is an independent risk factor for death and a predictor of exposure. As a third example, in a non-randomized community- based study of the effect of AZT on times to AIDS in HIV-infected subjects, subjects with low T4 lymphocyte counts or with symptoms of HIV infections (e.g. thrush) are more likely to develop AIDS and to receive treatment with AZT. Thus low T4 count and symptoms of HIV infection are risk factors for AIDS and predictors of AZT exposure. As a final example, in occupational mortality studies, unhealthy workers who terminate employment early are at increased risk of death compared to other workers and receive no further exposure to the agent under study. Therefore, the time-dependent covariate ‘employment status’ is an independent risk factor for death and a piedictor of exposure to the study agent. It may be important to analyse the data from any of the above studies using the approach presented in this paper.

To begin I first review the concept of causal confounding in point exposure studies.’ -7

1. A REVIEW OF CAUSAL CONFOUNDING IN POINT EXPOSURE STUDIES

Consider a point exposure follow-up study in which at the start of follow-up t , each of N study subjects is either exposed (written e ( t l ) ) or unexposed (C(tl)). Vital status is recorded at the end of the follow-up t,. The investigator observes the empirical distribution of exposure and mortality. For example, p[d < t , I e ( t l ) ] is the mortality rate among the exposed, i.e. the proportion of the exposed subjects who died over the study period. Here, d represents time of death. Until Section 10, we ignore sampling variability and make no distinction between sample proportions and population proportions. cRD = p [ d < t z l e ( t l ) ] -p[d <t21C(t,)] is the crude risk difference. Such observable quantities constitute the parameters of interest in descriptive epidemiology. In etiologic research, on the other hand, the parameters of interest are intrinsically unobservable. For example, Miettinen and Cook’ suggest the expression of causal parameters of interest in etiologic research in terms of comparisons between the observed numbers of cases that occurred in the exposed group (0) and the number of cases that one would have observed had that group been unexposed (i.e. the expected number of cases Ex). Specifically, we define the causal risk difference in the exposed to be O / N , - EJN, . Here, N, is the number of exposed subjects, OIN, is the observable parameter p [ d < t, 1 e ( t l ) ] , and Ex is unobservable, since we cannot observe the outcome of exposed subjects when unexposed.

Another commonly chosen causal parameter of interest is the causal risk difference. The causal risk difference is the difference between the mortality rate that we would have observed if the entire study population had been exposed and the rate that we would have observed if the entire study population had been unexposed.

Following Greenland and Robins,’ we say there is no confounding for the causal risk difference in the exposed if and only if the crude risk difference is equal to the causal risk difference in the exposed. As discussed by Greenland and Robins, there will be no confounding for the causal risk

CONTROL OF CONFOUNDING 68 1

difference in the exposed if the exposed and unexposed cohorts are partially exchangeable. (We say the exposed and unexposed cohorts are partially exchangeable if the mortality rate in the unexposed cohort equals the mortality rate that we would have observed in the exposed cohort in the absence of exposure.) In contrast, as discussed below, there will be no confounding for the causal risk difference (i.e. the crude risk difference will equal the causal risk difference) only if the exposed and unexposed cohorts are exchangeable. We say two groups are exchangeable if the mortality rate in the first group would equal that in the second had either (1) both groups been exposed or (2) both groups been unexposed. Exchangeability implies partial exchangeability.

One cannot empirically determine whether the exposed and unexposed groups are exchangeable or partially exchangeable. Nonetheless, at start of follow-up, if the unexposed and exposed cohorts differ on a strong empirical risk factor for death (e.g. age at start of follow-up) then, often, (a) the two groups are not exchangeable or even partially exchangeable, and (b) the crude risk difference fails to equal the causal risk difference or the causal risk difference in the exposed. In this setting, if the exposed and unexposed subcohorts of a given age are exchangeable, then (1) an age-specific empirical risk difference equals the causal risk difference (and the causal risk difference in the exposed) for the subset of the population of the corresponding age; (2) the identifiable internally standardized mortality difference with weights taken from the exposed population (the sMD) equals the causal risk difference for the entire exposed cohort;* and (3) as shown later, the identifiable standardized risk difference with weights taken from the entire population (sRD) equals the population causal risk difference. When propositions (a) and (b) and (1) to (3) above hold, we say that (a) there is no confounding for the age-specijc causal risk difference or the age-specific causal risk differences in the exposed, and (b) age is a confounder for both the causal risk difference in the exposed and the causal risk difference.

We now consider what is involved in extension of this approach to causal confounding to longitudinal studies. To help focus the discussion, consider a longitudinal observational study of the effect of oestrogen replacement therapy on the overall mortality of women who have experienced surgically induced menopause because of benign ovarian conditions. Specifically, suppose that we have entered into follow-up 2000 45-year-old women who experienced surgical menopause at calendar data t , . We record annual data on current vital status and current oestrogen exposure (coded as e if currently taking replacement oestrogens and d otherwise). Then, in analogy with our discussion of confounding in point exposure studies, we should like to answer the following questions. In a longitudinal study, what parameters represent the causal effect of replacement oestrogens, i.e. what are the analogues of causal risk difference and the causal risk difference in the exposed? What exchangeability conditions must hold so that we can compute these causal parameters from the empirical data on oestrogen exposure and mortality? If the requisite exchangeability conditions hold, how do we compute the causal parameters of interest from the empirical data, i.e. what is the analogue of the observable crude risk difference? If there exists a covariate, e.g. cholesterol level, that both predicts mortality and is associated with oestrogen replacement therapy, what exchangeability conditions must hold such that we can compute the causal parameter of interest from data on exposure, vital status, and cholesterol history? If these exchangeability conditions hold, what observable parameter equals the causal parameter of interest, i.e. what are the analogues of the sMD and sRD? In this paper, I shall attempt to answer these questions.

2. OVERALL VERSUS DIRECT EXPOSURE EFFECTS IN A LONGITUDINAL STUDY

Figure 1 represents the first three years of vital status data and the first two years of exposure data from the longitudinal study of the effects of replacement oestrogens on mortality described above,

682 JAMES ROBINS

270 (0-54

Figure 1. Measured graph 1 e = currently exposed to exogenous oestrogen I?= currently unexposed to exogenous oestrogen Whole numbers are the numbers of subjects who survive at the given time with a given exposure history Fractions in ( ) are conditional probabilities described in text Letters on a given internodal line linking nodes (circles) at times t, and t , , , refer to exposure measurements made at t ,

and has the following interpretation. At t,, 1200 (60 per cent) of the 2000 women with surgical menopause received oestrogens and 800 did not. At time t , (one year later), 900 (75 per cent) of the 1200 women who had received oestrogens at t , remained alive. Of these 900, 500 (56 per cent) continued oestrogens at t , while 400 stopped the medication. Of the 500 women who continued on oestrogens, 270 (54 per cent) survived until the end of follow-up at t,. Of the 400 women who stopped taking oestrogens at t,, 195 survived to t , . (I have chosen these implausibly high death rates for pedagogic purposes.) Until Section 9, we suppose that t , is the only time at which women change their oestrogen dosage. Until Section 10, we ignore sampling variability. Therefore, the terms ‘identifiable parameter’, ‘observable parameter’, ‘empirical parameter’, and ‘computable parameter’ can and will be used interchangeably.

If we consider follow-up only through t,, then the longitudinal study represented in Figure 1 is equivalent to a point exposure study. We shall later take advantage of this fact to contrast and compare the rules for confounding in point exposure studies with those in longitudinal studies.

As discussed in the introduction, two commonly chosen parameters of causal interest in point exposure studies are the causal risk difference and the causal risk difference in the exposed. For the

CONTROL OF CONFOUNDING 683

causal risk difference to be a well-defined parameter, it is necessary that both the numbers of deaths that would have occurred among the exposed population in the absence of exposure and those that would have occurred in the unexposed population in the presence of exposure are well- defined numbers. Therefore, we shall entertain the following deterministic model for mortality applicable to both our point exposure and our longitudinal study. We suppose, as in References 8-1 1 , that each subject i has four, possibly distinct, deterministic death times di,,=(,,), di,,=(,&, di,,=(ge), di,,=(&), where, for example, di,,=(;) is the time subject i would have died in a hypothetical controlled study, labelled G =(@, in which at t , the subject was unexposed, and at t , (if still alive) the subject would be exposed. We sometimes write G=(ee) as Gee.

We assume if di,G=(e;)<tZ, then di ,G=(ee)=di ,G=(ee) . For example, if subject i would die (when exposed at tl) at a time t less than t , , she would die at t both in a study in which she was to be exposed to oestrogen at t , and at t2 (i.e. the study G = (ee)) and in a study in which she was to be exposed at t , but not at t , (i.e. the study G = (eF)). In addition, we suppose that a subject’s time of death is uninfluenced by the exposures received by any other subject. This causal model is an extension of Rubin’s causal model’, to longitudinal studies with time-dependent exposures.

In this notation p[d,=(,,, < t 2 ] =p[d,=(,,-, < t , ] is. the proportion of the study population who would die before t , if exposed at t,. Thus, the causal risk difference (in the point exposure study with follow-up ending at t,) is, by definition, p[d,=(, ,) < t,] - p [ d , = ( z ) < t,]. Furthermore, the proportion of those exposed at t , in the observed study who would have died by t , if unexposed, i.e. EJN,, is p[dG=(;) < t 2 l e ( t l ) ] . In addition, the observed proportion of those exposed at t , who die before t , can be written ~ [ d , = ( ~ , ) < t , l e ( t , ) ] . Thus the causal risk difference in the exposed can be written as

pEdG=(ee) < t 2 le(tl)l -pEdG=(; ) < l 2 I e(tl)l. Any probability statement without a subscripted G will refer to outcomes in the observed study. For example, p [ d < t , ie( t , ) ] is the proportion of study subjects exposed at t , in the observed study who are observed to die before t,. Note p[d< t z Ie ( t , ) ]=p[dG=( , , )< t , ) e ( t1 ) ] .

We shall find it m6re convenient to work in terms of survival probabilities than death probabilities. As a comparison of survival probabilities we can write the causal risk difference as

A natural measure of the causal effect of exposure in our longitudinal study is a comparison of the survival curves (or mortality curves) of the hypothetical studies Gee and G,, i.e. p [ d G = ( ~ ) > t k ] - p [ d G = ( , , , > t a ] , k ~ { 2 , 3 } . But, as we have s e e n , ~ [ d ~ = ( ~ ) > t ~ l - p C d ~ = ( ~ ~ ) > t ~ l is the causal risk difference from the point exposure study with follow-up ending at t,. The new causal parameter p[d,=(,-;;, > t ,] -p[d,=(,,) > t , ] , which we call the extended causal risk diference, is the difference between the proportion of the population who die by t , in the hypothetical study Gee and the proportion who die by t , in the hypothetical study G;. The extended causal risk difference is the natural generalization of the causal risk difference parameter to studies that have sustained exposure periods. (In contrast, the causal risk difference in the exposed does not have a natural generalization to longitudinal studies that have time-dependent exposure^.^)

(Alternative measures of exposure effect would include a comparison of the survival curves of the hypothetical studies G;, and G,; with those of studies G z and Gee. These comparisons will often be of less interest if the dose response is monotone.)

The extended causal risk difference represents the ouerall (total) effect of exposure on mortality through t 3 with no control for the potential intermediate variable cholesterol history since, by the definition of the hypothetical controlled trials G=(ee) and G = ( Z ) under comparison, the investigator controls (i.e. determines) exposure status at each time but does not control cholesterol status (i.e. nature determines cholesterol status).

P C ~ G = ( Z ) >t, l - ~ C d c = ( e e ) > t21.

684 JAMES ROBINS

If, on the other hand, the causal parameter of interest was the direct effect of exposure controlling for (the potential intermediate variable) cholesterol history, we would wish to compare the mortality differences at t2 and t 3 in hypothetical studies in which the investigator controls both exposure and cholesterol leve1.8-”*’3*’4 A s one measure of the direct effect of exposure, we could compare the survival curves of the following two hypothetical studies. In study 1, the investigator exposes each (surviving) subject to exogenous oestrogen at times t , and t , and forces each subject’s cholesterol level at t , to be within the normal range (e.g. perhaps by prescription of a drug whose effect is to maintain cholesterol level within the normal range without an affect on any other metabolic pathway). In the second study, the investigator prevents exposure to oestrogens at t , and t , and again forces cholesterol at t , to be within the normal range. Letting rrepresent normal cholesterol level and 1 represent elevated cholesterol level, we use Gee,crz, to refer to the first study, G , c t , , to refer to the second, and

P [ d G = ( ~ ) , l ( t 2 ) > t k l - P C d G = ( e e ) , l ( 1 z ) > hl, kE(2, 3 1 9

to refer to the difference in their survival curves. As a second measure of the direct effect of exposure we could compare the survival curves of the studies and Gz,l(r2), where, for example, the hypothetical study Gee,l(tz,, is identical to the hypothetical study Gee,ztz), except that the investigator forces an elevated cholesterol level at t , for each subject (by, if necessary, administration of some other appropriate drug).

If exposure has a direct effect on mortality controlling for cholesterol history, we say exposure is a causal risk factor for death controlling for cholesterol history.

Clinical and public health interest would likely centre on the overall effect of oestrogen on survival (assuming a safe and effective cholesterol lowering drug is unavailable). On the other hand a biologist, interested in the mechanism of action of oestrogen, would also have interest in the direct effect of oestrogen. In this paper we largely restrict attention to the causal risk difference and extended causal risk difference - parameters that represent the overall effect of exposure on mortality. As we shall see later, the direct and overall effect of exposure can differ when cholesterol level at t , is an intermediate variable on the causal pathway from oestrogen exposure to death.

3. RANDOMIZED GRAPHS, CONFOUNDING, AND THE EXTENDED CRUDE RISK DIFFERENCE

We now determine exchangeability assumptions under which the causal risk difference and the extended causal risk difference can be computed from data on exposure and disease.

First, define a crude population parameter to be any population parameter that we can compute whenever we have data on exposure and disease for each study subject in the population. For example, the crude risk difference is p [ d > t , J P ( t , ) ] - p [d> t , l e ( t , ) l .

In Section 1, we noted that the causal risk difference equals the observable crude risk difference if, at time of exposure, the exposed and unexposed comparison groups were exchangeable. We now define the exchangeability conditions that must be met if the extended causal risk diference is to equal a crude parameter.

To do so, we need to generalize the definition of exchangeability given in the introduction.

Dejinition of exchangeabili’ty

Two subgroups of the population alive at t, in the observed study are exchangeable at t k if the survival curves of the two subgroups are the same in any hypothetical controlled study in which all members of the two subgroups receive the same exposure history from t k to end of follow-up.


(Here, we assume that the exposures received by the two subgroups prior to t k are those received in the actual observed study.) In general, if the two subgroups differ on risk factors for death at time t k , the two subgroups are not exchangeable at that time.

Example

Consider the subgroups of the population respectively exposed and not exposed at t , in the observed study represented in Figure 1. These two subgroups are exchangeable at t , with follow- up through t , if the two subgroups have the same survival curves in the hypothetical studies G = (ee), C(e4, G = (ge), and G = (24, i.e.

pCdG > t k l e ( t l ) l = p C d G > t k l e(tl)l for all GE{G=(ee), G=(Ce), G=(eF), G=(E)} , t k E ( t 2 , t,}. (1)

If (1) holds then the causal risk difference equals the crude risk difference. (See Theorem A.l of Appendix I.)

Henceforth, we refer to Figure 1 as measured graph 1 to be consistent with the nomenclature used in References 8-1 1,13. We say that measured graph 1 is randomized through t , if (1) holds.

If first, (1) holds, and second there is exchangeability at t , between any two subgroups who differ in exposure at t , but have a common exposure at t,, i.e.

pCd~>t3 le ( t , ) , 4t2)1 = P [ d ~ > t ~ l e . ( h ) , %)I, G€{G=(@, G=(ee)}, (2)

p[dG>r3le(t1), @,)I =pCd,> t,le(t,), 2(t2)1, G+G=(Z), G=(@}, (3) and

then we say measured graph 1 is randomized.

parameter If measured graph 1 is randomized, then the extended causal risk difference equals the crude

pCd> t2l~(tl)l P[d>t , ld( t , ) , ~ ( t 2 ) 1 - ~ C d > t ~ I ~ ( t i ) l P [d> t , I e ( t~ ) , e(t2)l

= (0.75) (0.57) - (0.75) (0.54) = 0.023,

which we call the extended crude risk difference. (See Theorem A.l of Appendix I.) Somewhat informally, measured graph 1 is randomized if among a group of the population

alive (in the observed study) at t , with a given exposure history through t,- ,, the subgroup exposed at t, does not differ from that unexposed at t , on the distribution of unmeasured risk factors for death at t,. Note, for measured graph 1 to be randomized, we do not require that the subset of the population exposed at t , and surviving to t , in the observed study is exchangeable at time t , with the subset of the population unexposed at t , and surviving to t,.

We now provide a definition of causal confounding appropriate for both point exposure and longitudinal studies:

DeJinition of causal confounding

There is confounding (no confounding) for a particular causal parameter of interest if that parameter does not equal (does equal) a crude population parameter.

It follows that there is no confounding for the causal risk difference if measured graph 1 is randomized through t , and there is no confounding for the extended causal risk difference if measured graph 1 is randomized.

686 JAMES ROBINS

I

\ I

\ \

Figure 2. Measured graph 2 e=currently exposed to exogenous oestrogen i?=currently unexposed to exogenous oestrogen r= normal or low blood cholesterol level 1 =elevated blood cholesterol level Whole numbers are the numbers of subjects who survive at the given time with a given exposure and cholesterol history Fractions in ( ) are conditional probabilities defined in text Letters on a given internodal line linking nodes (circles) at times t, and t,+ refer to exposure and cholesterol measurements

made at t ,

4. CONTROL OF CONFOUNDING IN A LONGITUDINAL STUDY

Suppose an investigator is unwilling to assume that measured graph 1 is randomized because he/she believes that physicians are less likely to prescribe oestrogens to women with high cholesterol (a known causal risk factor for death from heart disease) than to women with low cholesterol. This investigator would then be unwilling to accept either that the observable crude risk difference equals the causal risk difference or that the observable extended crude risk difference equals the extended causal risk difference. Suppose now that the investigator has data on each subject’s cholesterol level measured at times t , and t,. Below we define conditions under which the investigator could compute the causal risk difference and the extended causal risk difference from data on exposure, cholesterol, and vital status.

Measured graph 2 in Figure 2 represents data from the study shown in Figure 1, except that data on cholesterol level measured at t , and t , are now available. Symbol his normal (or low) cholesterol and 1 is elevated cholesterol. Reading from graph 2 we see that of the 2000 subjects in the study, 1400 (70 per cent) had elevated cholesterol levels at t,. Of the 600 subjects in the study


with normal cholesterols at t,, 360 (60 per cent) received post-menopausal oestrogens at that time. Of these 360 women, 300 (83 per cent) survived to t,. Of these 300 survivors, 150 (50 per cent) had normal cholesterol when measured at t,. Of these 150,100 (67 per cent) were exposed to oestrogens at t,. Of these 100,90 (90 per cent) survived to t3. The rest of the graph has a similar interpretation.

With data on cholesterol (but on no other covariate) available, we call Figure 2 the ‘full data’ and Figure 1 the ‘crude data’.

If subsets of the s t u e population with identical cholesterol levels but different exposure levels at t , are exchangeable at t,, i.e.

pCdG > t k I L(t 11, (t 1 )I = pCdG > tk I Yt 1 1 9 e(tl )I,

L ( t l ) ~ { K t l ) , 9t,>>, GE(Gee, G , G e , Gie},

(4)

then we can compute the causal risk difference from data on exposure, cholesterol, and vital status. Specifically, the causal risk difference equals the observable standardized risk difference with weights taken from the entire population (sRD), where

sRD =p[l(t,)]RD, +p[l(tl)]R&

=0~7[(1-071)-(1-0*71)]+0~3[(1-0~83)-(1-0~83)]=0 (5 )

and e.g. RD,=p[d<t , \e ( t , ) , E(tl)]-~[d<t212(tl), l(tl)] is the observable risk difference in stratum 1. (This result follows from Theorem A.l in Appendix I.)

(In (4) we have used the notational convention that L(tk) is a particular cholesterol history

If (4) holds, we say measured graph 2 is randomized through t,. If first (4) holds, and second there is exchangeability at t, between any two subgroups who

differ in exposure at t , but have a common exposure at t, and a common cholesterol history through t , i.e.

from t , through t k . )

p[dG> t3IL(tz), E(ti), e(tz)l=P[d~)t3It(t2), E(ti), F(t211, (6)

W 2 ) 4 @ 1 ) , @2)), (@l), 4 t 2 h ( k ) , @,)), (@A, w% we say that measured graph 2 is randomized.

data on exposure, cholesterol, and vital status history. Specifically, If measured graph 2 is randomized, we can compute the extended causal risk difference from

688 JAMES ROBINS

The extended causal risk difference equals 0.429 -0.383 = 0.046. (See Theorem A.l in Appendix I.) In (7) and (8) we have used the notational convention that when L(t 1) and L(t2) appear in the

same expression, L(t , ) will bz the initial part of L(t2) through time t , . For example, consider the four terms in the expression in set braces in (7) when L(t , )=(@,) , qt,)). From Figure 2, the four terms are p [ q t l ) ] = 0 . 3 , F[d>tzIq t , ) , e ( t1) ]=0 .83 , p [ [ t , ) , @t,)Id>t, , [ t l ) , e ( t , ) ] =0.5, and

We define the extended standardized risk diflerence to be the observable parameter given by the difference between (8 ) and (7).

Note that, in a sufficiently large study (so that we can ignore sampling variability), if a physician’s decision to place a woman on oestrogen at time t k is based only on knowledge of the woman’s past oestrogen treatment history through t k - 1 and cholesterol history from t , to t k

(measured as a sequence of binary variables), then measured graph 2 will be randomized (provided, of course, that women treated by those physicians mosl disposed to prescribe estrogens do not differ on unmeasured risk factors from the other women in the cohort). On the other hand, if the physician’s decision is also influenced by either the woman’s blood pressure history or cholesterol history measured as a continuous variable, then measured graph 2 will not be randomized.

p [ d > t , l @ , ) , @,I, e ( t A e(t2)l =0.9.

5. CONFOUNDING BY A COVARIATE 1

We now define circumstances under which it is legitimate to say that there is confounding for a particular causal parameter by a given covariate 1.

Definition

Given a particular (possibly time-dependent) covariate 1, we say that a parameter is 1-identifiable if we can compute the parameter from the data on exposure, I , and vital status history.

Example

Whether or not measured graph 2 is randomized, it follows from the definition that we can compute the standardized risk difference (sRD) and the extended standardized risk difference from data on exposure, 1 and vital status history. Thus these parameters are 1-identifiable. Therefore, if measured graph 2 is randomized through t , , the causal risk difference is I-identifiable (since it equals the standardized risk difference); if measured graph 2 is randomized, then the extended causal risk difference is I-identifiable (since it equals the extended standardized risk difference).

Definition

1 is a confounder for an I-identifiable parameter of interest if the parameter does not equal a crude parameter.

(We choose not to define circumstances under which it is legitimate to say that 1 is a confounder for parameters that are not I-identifiable. The motivation for this choice is the observation that if the causal parameter of interest is not 1-identifiable then, even given data on the potential confounder 1, the parameter of interest cannot be computed.)

Throughout the remainder of this paper we suppose that measured graph 2 is randomized, and thus the causal risk difference equals sRD and the extended causal risk difference equals the extended sRD. Then, it follows that 1 is a confounder for the causal risk difference if and only if sRD # cRD, and 1 is a confounder for the extended causal risk difference’if and only if the extended crude risk difference does not equal the extended sRD.


Example

In Figure 2, sRD = cRD = 0, so I is not a confounder for the causal risk difference. On the other hand, the extended crude risk difference (0.023) does not equal the extended standardized risk difference (0.046), so 1 is a confounder for the extended causal risk difference.

6. CONDITIONS FOR CONFOUNDING

We now determine the empirical conditions that the associations of the covariate with exposure and/or disease in the study population must satisfy in order for a covariate to be a non-confounder for (1) the causal risk difference and/or (2) the extended causal risk difference, i.e. in order for (1) sRD = cRD and/or (2) for the extended crude risk difference to equal the extended sRD.

We have sRD=cRD if either (a) 1 is not an empirical risk factor in both the exposed and unexposed, i.e.

and

PCd<t,Il(t,), W I =pCd<t,liit,), ?(tl)l, or (b) e and 1 are not associated at start of follow-up, i.e.

PCe(tl)l4tl)I =pCe(t,)I tit,)]. (10)

In our example sRD=cRD, since (10) holds on measured graph 2.

controlling for exposure history, i.e. by definition, if (9) holds and The extended sRD equals the extended cRD if either (a) I-history is not a risk factor for death

(11) p[d<t,lLi(t,), E(t2), d>t,I=~Cd<t3IL2(t,), E(t2), d > t J for any L,(t,), L2(t2), and E(t2), where E(t,) is an arbitrary exposure history through t,, and L,(t2) and L2(t2) are any two different cholesterol histories through t,; or (b) I-history is not a predictor of exposure, where we define 1-history not to be a predictor of exposure if (10) holds and for all E ( t 2 )

PCE(t2) I Ll(t2h E(tl), d > t 2 ) l = PCE(t2) I L2(t2), E(tl), d > t21 (12) where E(t,) is the initial part of E(t2) , e.g. if E( t2 )= [2(tl), e(t,)], then E( t , ) = [2(tl)]. For a proof see Corollary A.l and Theorem A.3 of Appendix 11.

In words, I-history is not a predictor of exposure if, among a set of subjects with a given exposure history through tk - , who are alive at tk, the probability of exposure at t k does not depend on cholesterol history through tk

690 JAMES ROBINS

As one might expect, the following two theorems are true:

Theorem

If measured graph 2 is randomized through C, and (9) or (10) holds, then measured graph 1 is randomized through t,.

Theorem

If measured graph 2 is randomized and I-history is not a risk factor for death controlling for exposure history or I-history is not a predictor of exposure, then measured graph 1 is randomized.

Proofs

See Theorem A.2 and Corollary A.2 of Appendix 11.

7. THE CONTROL O F CONFOUNDING BY COVARIATES THAT ARE BOTH CONFOUNDERS AND INTERMEDIATE VARIABLES

We have shown that cholesterol history is a confounder in our data for the overall effect of - oestrogen exposure on mortality (as measured by the extended causal risk difference). Further- more, we have shown that we can control for this confounding by using the extended standardized risk difference to compute the extended causal risk difference. In this section, we shall demonstrate that this remains true even when cholesterol history is an intermediate variable on the causal pathway from exposure to disease.

Formally, we say that cholesterol history is an intermediate variable on the causal pathway from oestrogen exposure to death if (a) cholesterol level at t , is a causal risk factor for death controlling for exposure history, i.e. if for example p [ d G = ( q , c t , , > t,] # ~ [ d ~ = ( = ) , ~ ( ~ , ) > t,]; and (b) exposure history is a causal risk factor for cholesterol level at t,, i.e. in our formalism, P[L( tz )G=(z) ] # P [ L ( t & = ( & ) ] , where L(t,)i,G=(eq is the cholesterol history through t2 for subject i in that hypothetical study G=(C, 9, and p [ L ( t , ) G = ( a ] is the proportion of the study population who would have a particular cholesterol history L(t,) through t , in that hypothetical study. (In the above definition we have assumed that oestrogen exposure at t l has no influence on measured cholesterol level at t , , since the cholesterol measurement is made prior to the oestrogen treatment decision.)

Before proceeding, it is important to recognize the different meanings of the word ‘controlling’ in the two expressions: ‘I-history (i.e. cholesterol history) is not an empirical risk factor for death controlling for exposure history’; and ‘I-history is not a causal risk factor for death controlling for exposure history.’ The former is a statement about the empirical (i.e. observable) world-a statement that (9) and (1 1) hold. We can translate this use of ‘controlling for exposure history’ into the equivalent terms: ‘controlling for exposure history in the analysis’, ‘with statistical control for exposure history’, ‘stratifying on exposure history’, ‘adjusting for exposure history in the analysis’, ‘conditional on observed exposure history’. On the other hand, the latter expression is a causal


statement that compares survival curves of hypothetical controlled trials. ‘I-history is not a causal risk factor for death controlling for exposure history’ implies that the survival curves are identical in, as one example, the following two studies: a hypothetical study in which an investigator controlled each subject’s cholesterol history at t , and t , such that he/she kept that cholesterol in the normal range at final t , and prevented all exposure to exogenous oestrogens; and a second hypothetical study in which he/she forced each subject’s cholesterol level to remain elevated at t , and t , and again prevented all exposure to exogenous oestrogens. That is, p[d,=(~-,(jjp t k ] =p[d,=cz, ,(n, > t k } in obvious notation. This use of ‘controlling’ for exposure history is in the sense of ‘manipulating’ or ‘determining’ exposure history in a‘hypothetical controlled trial.

Appendix I11 provides exchangeability conditions under which we can estimate from empirical data on exposure, vital status, and cholesterol both the direct effect of exposure on mortality controlling for cholesterol and the direct effect of cholesterol on mortality controlling for exposure. We call these exchangeability conditions the exchangeability conditions for direct effects.

In Appendix 111, we prove a theorem showing that if the exchangeability conditions for direct effects hold, then I-history is not a causal risk factor for death controlling for exposure history if and only if 1-history is not an empirical risk factor for death controlling for exposure (i.e. (9) and ( 1 1 ) hold). Furthermore, the theorem remains true with the roles of I-history and exposure history reversed.

This theorem makes clear why there is often confusion with the two different meanings for ‘controlling for exposure’ discussed above; under the assumption of exchangeability for direct effects, each implies the other. (When the exchangeability conditions for direct effects do not hold, we may observe, as demonstrated in Example 1 of Reference 8, that l-history may have no direct causal effect on mortality controlling for exposure history and yet I-history is an empirical risk factor for death controlling for exposure.) Henceforth we shall assume that the exchangeability conditions for direct effects hold. (Theorem A.4 of Appendix I11 also implies that, under the exchangeability conditions for direct effects, if, as in our data, cholesterol level at t , is an empirical risk factor for death controlling for exposure at t l and t , and cholesterol at t , , then cholesterol level at t , is a causal risk factor for death controlling for exposure history, i.e. condition (a) in the definition of intermediate variable holds.)

In our data, exposure is not an empirical risk factor for death controlling for cholesterol history and thus exposure has no direct effect on mortality controlling for cholesterol. For example,

Therefore, under the assumptions of randomization for measured graph 2 and the exchangeability conditions for direct effects, (1) exposure has no direct effect on mortality controlling for cholesterol level, but (2) exposure has an overall effect on mortality (i.e. the extended sRD =extended causal risk difference =0.046). It is intuitively clear, and formally shown in Section 8 of Reference 9, that these two conditions imply that cholesterol is an intermediate variable on the causal pathway from exposure to death (i.e. conditions (a) and (b) in the definition of an intermediate variable given above hold). (Note that under the specific exchangeability assumptions made above, the fact that exposure at t , is an empirical predictor of cholesterol level at t,, when stratifying on cholesterol level at t,, would not have been by itself sufJicient to prove that exposure is a causal risk factor for cholesterol level at t,.)

692 JAMES ROBINS

In summary, the use of the extended standardized risk difference has allowed control of confounding by a covariate, cholesterol history, that is simultaneously a confounder for the overall effect of exposure and an intermediate variable on the causal pathway from exposure to death.

8. A LONGITUDINAL STUDY WITH LONG-TERM FOLLOW-UP

Suppose in our longitudinal study, follow-up continues until time t,, where t , > t,, and we record data on blood cholesterol level, exogenous oestrogen exposure, and vital status at times t,, t2, . . . , t,. For any exposure history E,(ts), let G = El denote the hypothetical controlled trial in which each subject alive at t, receives the exposure level indicated by the exposure history El(ts). For convenience, we adopt the notational convention that G = I? denotes the hypothetical study that involves withholding exposure to exogenous oestrogen at all times; and in this section only, G = E (where E is not iubscripted) is the hypothetical controlled trial that involves continuous exposure to oestrogen at all times t,. For t k < ts, let the extended causal risk difference through t k be p[dG=,-> t k ] - P [ d G = E > t k ] , the difference between the proportion of the population who would survive to t k in the study G = I? and the proportion surviving to tk in the study G = E. Define measured graph 1 (when extended to t,) to be randomized through t k if

= E l > tk I l ( t s - 11, e(ts)l = pCdG = El > tk I 1 1 3 q t s ) l (13)

for all ts < tk < ts, E,(ts- ,), and all G = E l such that the initial part of El is E,(ts- ,), and E,(t,- ,) is an arbitrary exposure history through ts- ,. If measured graph 1 is randomized, we can compute the extended causal risk difference through tk from data on exposure and vital status history as

where E(t,-,) is, in this section only, the history of continuous oestrogen exposure from t , through tm-,. Expression (14) is called the extended crude risk difference through tk.

Define measured graph 2 (when extended to t,) to be randomized through tk if

p C d G = E , > t k I E l ( t s - 11, L(ts)? e ( t s ) l = p C d G = E , > t k I E l ( t s - l ) , L(ts), q t s ) l (15)

for all t , < tk < t,, El@,- 1), at,), and G = El with initial segment El(&- Even if measured graph 1 is not randomized, if measured graph 2 (when extended to ts) is randomized through tk, we can compute the extended causal risk difference through tk from data on cholesterol history, exposure history, and vital status history as

(16) where again the sum is over all possible cholesterol histories L(tk.9 and L(t,) and L(t,) are the initial parts of the given L(tk). Expression (16) is called the extended standardized risk difference through tk (In the terminology used in References 8-11, (16) is the result of applying the G-computation algorithm to measured graph 2.)


Given that measured graph 2 is randomized through t,, measured graph 1 will be randomized through t, if cholesterol history is not an empirical risk factor for death controlling for exposure history, i.e.

(17)

P I E l ( t k ) I L l ( t k ) , d > t k , 111 = p [ E l ( t k ) I d > t k , L2(tk) , E l ( t k - 1)19 tkGts . (18)

PCd < l k 1 L l ( t k - 1), E l ( t k - 1)1 = pCd < tk 1 LZ(tk - 11, E l ( t k - 1)1, t k < t s ,

or cholesterol history is not a predictor of exposure history, i.e.

For a proof see Theorem A.2 and Corollary A.2 in Appendix 11. If (17) or (18) holds, then the extended standardized risk difference through ts equals the

extended crude risk difference through t,. For a proof see Corollary A.l and Theorem A.3 in Appendix 11.

9. A LONGITUDINAL STUDY WITH INFREQUENT MEASUREMENTS

Suppose that in our longitudinal study (1) follow-up occurred through t,, (2) we collected data on current oestrogen exposure at t,, t, and t,, and (3) measured graph 1 (extended to t,) was randomized. Then, as discussed above, we can compute the extended causal risk difference through t , from (14).

Now suppose that we had obtained data on exposure status only at times t , and t,, but not at t,. Then we can represent the data recorded for data analysis by Figure 1 modified so that t, and t , are relabelled t , and t,, respectively. The modified Figure 1 will not in general be randomized if (the unrecorded) exposure status at t , is a causal risk factor for mortality at t, controlling for exposure at t l and t,. This lack of randomization follows from the fact that it will often be the case that a higher proportion of the subset exposed at t l and t , will have had exposure at t , than the subset exposed at t l and unexposed at t,. Therefore, these two subsets are not exchangeable at t,, and so the modified figure is not randomized.

It follows that, even if the unmodified Figure 1 is randomized, if we had collected exposure data at intervals of 2At (with At = t, - t , = t , - t,) rather than at intervals of At, the extended crude risk difference applied to the data in the modified Figure 1 will be biased for the extended causal risk difference. Nonetheless, the magnitude of the bias is negligible when the fraction of subjects who change their exposure status in any interval of length At is small.

Therefore, in realistic studies, we would wish to choose the time interval between exposure measurements sufficiently short that any bias attributable to the fact that subjects can change their exposure status between measurements is small. How short we must make this interval depends on the subject matter under study.

10. THE INTRODUCTION OF SAMPLING VARIABILITY

In the study shown in measured graph 1,300 of 1200 subjects exposed at t , die before t,. Then, according to our deterministic model, we know that p [ d c t2 I e(t ,)] is exactly 300/1200 = 025. We have no sampling variability since (1) each exposed subject’s outcome is predetermined and (2) we have not assumed that our study population is a sample drawn from a larger population.

In contrast, the standard approach most epidemiologists take is to report a binomial confidence interval of 0.25 f 1*96[(O-25)(0.75)/200]’’2 for the unknown parameter p[d< tz le( t l ) ] . The model implicit in the standard approach is as follows:

694 JAMES ROBINS

Superpopulation model

(1) The study population constitutes a random sample from a conceptually infinite superpopu-

(2) All inferences concern parameters of the superpopulation.

For example, the parameter p[d< t , l e ( t , ) ] is the proportion of subjects exposed at t , in the superpopulation who died by t,, and p [ d < t , l e ( t l ) ] =0-25 is the proportion of the (sampled) observed study subjects exposed at t , who die by t,. In this sampling model the number of subjects exposed at t , who die before t , is a binomial random variable (upon hypothetical resampling of 1200 exposed study subjects from the superpopulation). Since, in most epidemiologic studies, study subjects do not constitute a random sample from any near-infinite population, superpopulation models are fictions. A superpopulation model nonetheless has frequent use for the following reason. An investigator often wishes to generalize his or her findings from the observed study population to some larger population. For example, an investigator who considers a recommen- dation of public health intervention would hope to study the population that represents the population of potential recipients of that intervention. The simplest possible model considers the study population as a random sample of a larger population of potential recipients of the intervention.

Henceforth, we suppose random sampling of the observed study population from an infinite superpopulation and that the causal parameters of interest are those of the superpopulation. We then define a measured graph as randomized if and only if our definition of a randomized graph holds for the superpopulation. Then, even were measured graph 1 randomized, chance associations of exposure with unmeasured risk factors may exist in the observed study at t , due to sampling variability. Under this definition, if a physician’s decision to place a woman on oestrogen at time t , is based only on knowledge of the woman’s past oestrogen treatment history through tk-, and cholesterol history from t , to t, measured as a sequence of binary variables, then measured graph 2 will be randomized, regardless of the sample size (provided that women treated by those physicians most disposed to prescribe estrogens do not differ systematically on unmeasured risk factors from other cohort members).

Under this sampling model, the fractions written in parentheses on Figures 1 and 2 are sample proportions and are thus the non-parametric maximum likelihood estimators (NPMLE) of the corresponding superpopulation proportions. It follows, therefore, that if Figure 2 is randomized through tk, we obtain the NPMLE of the superpopulation extended causal risk difference (through t,) by (16) with population proportions replaced by sample proportions. To derive confidence intervals for the NPMLE of the extended causal risk difference through tk, we need to derive consistent estimators for the asymptotic variance of the NPMLE. Although we can derive analytic expressions for this variance, such expressions become unwieldy if k is greater than 5 or so. In practice, therefore, we usually rely on resampling methods such as the bootstrap to estimate the variance.

lation.

11. MODEL-BASED ESTIMATION O F THE EXTENDED CAUSAL RISK DIFFERENCE

If follow-up proceeds for a large number of time periods and/or the exposure or confounder are polytomous or continuous, the NPMLE of the extended causal risk difference through end of follow-up ts (equivalently, the extended standardized risk difference through ts) will be undefined due to ‘sparse data’ even in a large data set. In such a case, we must resort to the use of statistical models. The most straightforward approach would be to use parametric or semi-parametric


models for the population parameters

and

As an example, a model for (19) would be the discrete time Cox proportional hazards model

where Zlttm- is an indicator variable that takes the value 1 if the subject has high cholesterol at time t,- and is zero otherwise; ce(t,- 1) is cumulative oestrogen exposure from the start of follow- up through time tm- 1; and is a time-specific constant. The parameters can be estimated by logistic regression.

The extended standardized risk difference through any time t k can then be estimated by substituting the ‘fitted values’ of the population proportions in (19) and (20) into (16). (When the number of possible L(tk) histories that must be summed over in evaluating (16) is very large, a Monte-Carlo approximation may be employed as in References 8-1 1.)

Unfortunately, as is shown in References 9 and 13, this approach is seriously non-robust to model misspecification. Specifically, even under the null hypothesis of no exposure effect on mortality (i.e. the extended causal risk difference through t k is zero for all t k ) , the estimated extended causal risk difference (based on substituting the estimated proportions into (16)) may converge in probability to a quantity different from zero when (as is inevitable) the models for the proportions in (19) and (20) are misspecified.

In Reference 13, I develop a more robust approach to model-based estimation of the extended causal difference based on a new class of failure-time models, the structural nested independence failure-time models. If 1 is discrete, these models can be estimated using a class of semi-parametric estimators, the G-estimators, that, even in sparse data, remain unbiased for the extended causal risk difference under the null hypothesis of no exposure effect. G-estimators are closely related to the asymptotically distribution-free G-null test introduced in References 8-1 1. If 1 is continuous, then smooth-estimated-propensity G-estimators, regression G-estimators, or the parametric maximum likelihood estimator can be used to estimate the parameters of structural nested independence failure-time models.

12. SUMMARY AND EXTENSIONS

The main result of this paper is that use of the non-parametric maximum likelihood estimator (NPMLE) of the extended standardized risk difference allows for the non-parametric estimation of the overall effect of exposure on disease even in the presence of a covariate that is simultaneously a confounder and an intermediate variable. Of course, if follow-up proceeds for a large number of time periods and/or the exposure or confounder is polytomous or continuous, the NPMLE of the extended standardized risk difference will be undefined due to ‘sparse data’. In that case, as discussed in Section 11, the model-based estimation procedures provided in Reference 13 should be used.

Throughout this paper, we‘assumed the available data pertained to a dichotomous exposure and a dichotomous covariate. Furthermore, we assumed no misclassification of either exposure or the covariate cholesterol. References 8-1 1 and 13 generalize the results of this paper to multi-level or continuous exposures, covariates, and outcomes. References 10 and 13 discuss the effect of a non-differential misclassification of the exposure and/or the confounder on the estimation of the

696 JAMES ROBINS

extended causal risk difference. References 9-1 1 and 13 consider the effects of censoring and,death from competing risks. Reference 13 briefly considers the effects of missing exposure and/or covariate data. Reference 9 considers how one can use case-control data to make inferences concerning the extended causal risk difference. References 8-1 1 and 13 consider the estimation from observational data of the population survival curve of a hypothetical controlled trial based on ‘a dynamic estrogen treatment regime’ such as ‘take estrogen in the current period if and only if one’s current cholesterol level is within the normal range.’

Finally, suppose that the extended causal difference were assumed a priori to be identifiable from data on estrogen exposure, cholesterol, blood pressure, and vital status history. In Section 8 of Reference 9, I determine restrictions on the association of blood pressure history with estrogen exposure, cholesterol, and vital status history sufficient to allow one to identify the extended causal risk difference from data on estrogen, cholesterol, and vital status history alone. That is, I determine conditions under which blood pressure is not a confounder for the extended causal risk difference in the presence of data on cholesterol history.

APPENDIX I

We formalize the idea that a subjects L-and vital status history depends only on the estrogen treatments actually administered (and not on whether those treatments were administered in an observational study or in a hypothetical controlled trial) in the following

Assumption (a): Assume for any subject i with observed history [E,(t,), L(ts)] that the observed survival time d i > t s + l if and only if d i , G = E t > t s + l for El with initial segment El(ts) .

Theorem A . 1: the fundamental theorem

If (15) holds (i.e. measured graph 2 is randomized through t k ) then, under Assumption (a),

PCdG = E , > t k I E1(ts - I), U t S - d > t,], S 2 k > s


But

But

P [ d G = E 1 > t k I E l ( t s ) , Y t s ) l = ~ [ d G = E ~ > t , ~ E l ( t s ) , at,), d > t s + l l x P C ~ > t, + 1 lEl(ts), L(d1, by Assumption (a)

But, by Our induction assumption, P [ ~ G = E ~ > tklEl(ts), ats), d > t,+ 1] equals H(s+ 1). Therefore

PCdG=Ej > tk I 11, q t s - l), > tsl = c m+ l)PCd>ts+,IEl(ts), Yts)l

all Ut.)

Y t z - 1 )

with initial history

x P C L ( t S ) l W S - - 11, El@,- 11, d’tsl. But simple algebra shows the expression on the right side of the equal sign is H(s).

calculation similar to that above. The following are immediate corollaries. It only remains to show that the theorem is true for s = k - 1 which follows immediately from a

Corollary

If measured graph 2 is randomized through t,, then the extended causal risk difference through t , equals the extended standardized risk difference through tk. This follows by setting s= 1 in Theorem A.l where, by convention, E , ( t o ) and L(to) are set to zero.

Corollary

If measured graph 1 is randomized through tk, then the extended causal risk difference through t , equals the extended crude risk difference through t,. This latter corollary follows by considering the special case of Theorem A.l for which, at each time t,, the number of I levels is only one. Thus there is only a single L-history to sum over, and equation (15) reduces to equation (13).

Theorem A.l is a special case of Theorem AD. l of Reference 10.

APPENDIX I1

The results in this appendix are special cases of Theorems Fl-F4 of Reference 9.

Theorem A.2

If measured graph 2 (extended through ts) is randomized and (18) holds, then measured graph 1 is randomized.

Proof

By definition, measured graph 1 is randomized if (13) holds. Now the left side of (13) can be written

{ P C d G = E 1 >tkIEl( ts - l), L(ts), e ( t s ) l ~ [ L ( t s ) I e ( t s ) , I)]} (21) W.)

698 JAMES ROBINS

with the sum over the 2s possible cholesterol histories L(ts) up to t,. But (21) equals

1 {PCdG=El ? tkl l), L(ts), e(ts)l p[L(ts) I e(ts) , l)]} (22) LOS)

by the supposition that measured graph 2 is randomized (i.e. by (15)). Furthermore, (18) implies

pCL(ts)Ie(ts), E l k - 111 =PCYts)IW, E&s- 111.

Therefore (22) equals the right side of (13), proving the theorem.

Corollary A.l

If (18) holds, then the extended crude risk difference through t, equals th risk difference through t k .

Proof

extended sta dardized

Although we could prove the corollary directly from the definitions of the extended crude risk difference given in (14) and the extended standardized risk difference given in (16), we shall give a proof that elucidates further the relationship between’ our ‘causal model’ and the empirical world.

Suppose that measured graph 2 were randomized, i.e. (15) holds. Then the extended causal risk difference equals the extended standardized risk difference by the Theorem A.l of Appendix I. But, given the suppositions of the corollary, if measured graph 2 were randomized, then, by Theorem A.2, measured graph 1 would also be randomized, and so, by Theorem A.l, the extended causal risk difference would equal the extended crude risk difference. Therefore, if measured graph 2 is randomized and (18) holds, the extended crude risk difference must equal the extended standardized risk difference. Since we can never determine empirically whether or not measured graph 2 is indeed randomized (i.e. whether or not it is randomized or not is non-identifiable), it must be true, therefore, that the extended crude risk difference equals the extended standardized risk difference regardless of whether measured graph 2 is randomized. More technically, only the joint distribution of the random variables d , Ei(di), Li(di) is identifiable where, for example, Ei(di) is subject i’s exposure history up to their time of death di. (For notational convenience and without loss of generality, we assume all subjects die by end of follow-up.) But, it is clear that for any given joint distribution of the d , Ei(di) , Li(di), in the infinite superpopulation in Section 10, there exists a joint distribution for ( {d i ,G=E1; El E E}, d , Ei(di), Li(di)) for which measured graph 2 is randomized such that marginal distribution of the di, Ei(di), Li(di) is the given distribution. E is the set of all possible exposure histories through end of follow-up t,.

Theorem A.3

If (17) holds, then the extended standardized risk difference equals the extended crude risk difference.

Proof

A general expression for either term in (1 6) is


where again the sum is over all possible cholesterol histories q t k ) and L(t,) is the initial part of the given q t k ) . But if (1 7) holds, (23) equals

But

is the corresponding term in (14). Furthermore, the sum in (24) equals 1. Thus the theorem is proved.

Corollary A.2

If (17) holds and measured graph 2 (extended through ts) is randomized, then measured graph 1 is randomized.

Proof

We follow the proof of Theorem A.l through (21). It folIows from the fact that measured graph 2 is randomized (i.e. (1 5) ) that

pCdG = El > tk I 11, L(ts), e(ts)l = pCdG = E l ’ tk I - 11, qts ) l . (26)

(27) the corollary would be true. Note (27) will hold if we can show that the left hand side of the equation does not depend on L(t,). To show that (27) holds, we first note that, by Theorem A.l, ~ [ d , = ~ , > t , I E,(t , - ,), L(t,)] is given by (23) modified so that the products begin at rn = s + 1 rather than at m = 2 and p[L(t,)J is deleted, and the sum is taken over those q t k ) with initial segments L(t,). We now can follow the proof of Theorem A.3 to show that the modified (23) (and thus the left hand side of (27)) equals (25) modified so the product begins at rn = s + 1 and so, in particular, does not depend on L(t,).

Therefore, if we could show

pCdG = El > tk I E l ( t ~ - 11, L(t,)l = P [ ~ G = E ~ > t k I Ei(t, - I), d > ts),

APPENDIX I11

Given a particular exposure history E(t,) and cholesterol history q t , ) , let G = [E(t ,) , L(t,)] denote the hypothetical controlled trial in which we force each subject (while alive) to receive exposure and cholesterol history at t , and t , defined by E(t,) and L(t,).

Furthermore, given histories E(t2) and L(t,) and other histories E, ( t , ) and L,(t,), we define p [ d ~ = r ~ ~ ~ , , , L(t2)1 > t k ( E l ( t l ) , L,(t,)] as the probability of survival to t k in the study G = [E(t2), L(t2)] for the subset of the population who had exposure and cholesterol history E l @ , ) , L,(t,) through t , in the observed study.

Definition

We say that the exchangeability conditions for direct effects hold if (1) for all (E(t2), Yt,)), (El(t2), Ll(t2)), and ( E Z ( t 2 ) , LZ(t2))

d d G = [ E ( t 2 ) , L ( f 2 ) 1 > t k I E l ( t 1 ) , L1(t1)1 = P [ d G = [ E ( f 2 ) . r , ( t 2 ) ] ) t k I E 2 ( t l ) , Lz(t~)] for ke (2, 3}, (28)

700 JAMES ROBINS

and (2) for all (%), 4)), (.WZ), ~ l (b ) ) , (EAt2) , W,)) such that El(tl)=E2(tl)=E(tl) and Ll(tl)=L,(tl)=L(tl),

PCdc=[E(tl),L(r2),>t31 El(t2), ~51(t,)l =pCdG=[E(r2),L(r2)1>t3 lE~(tz), L2(t2)1 (29)

Remark

Consider the four subsets of the population defined by joint observed exposure and cholesterol level at t,. Equation (28) says these four subsets would have the same survival probability as one another at t, and t , in any hypothetical study in which we forced each member of the population to have the same prescribed exposure and cholesterol history at t , and (if alive) at t2 as each other member of the population.

Next, given any set of subjects alive at t , in the observed study all of whom had the same exposure and cholesterd status at t , , consider the four subsets defined by joint observed cholesterol and exposure level at t,. Equation (29) says that these four subsets would have the same proportion who survive to t , in any hypothetical study in which we force each subset to have the same prescribed. exposure and cholesterol level at t , (but in which exposure and cholesterol level at t , are as in the observed study).

Theorem A.4

Given that the exchangeability conditions for direct effects hold, l-history is not a causal risk factor for death controlling for exposure, i.e. by definition for all t k , E(t,), L,(t,), L,(t,),

~ ~ d c = [ E ( t 2 ) . L l ( r 2 ) ] l > t k = P C d G = [ E ( r 2 ) . L 2 ( r 2 ) , > t k l

if and only if I-history is not an empirical risk factor for death controllitg for exposure (i.e. (9) and (1 1) hold).

Prooj

This is an immediate consequence of Theorem AD.l of Reference 10, since, in the terminology of References 8-10, the exchangeability conditions for direct effects imply that the finer measured graph formed from measured graph 2 that has but one intranodal line per node is an R(D) SCISTG. Therefore, we can apply Theorem AD.l.

ACKNOWLEDGEMENTS

I would like to thank Sander Greenland, David Freedman and Paul Holland for their comments on earlier drafts. This work was suported in part by grants from the following organisations: NIEHS # 5 K04-ES00180, NIEHS # 5 P30 ES00002, American Lung Association # LA 3/22/85, the American Heart Association, and the Massachusetts Chapter of the American Heart Association.

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