marginal structural models and causal inference in epidemiolog.pdf

7/25/2019 Marginal Structural Models and Causal Inference in Epidemiolog.pdf

1/11

Marginal Structural Models and Causal Inference inEpidemiology

James M. Robins,1,2 Miguel Angel Hernan,1 and Babette Brumback2

In observational studies with exposures or treatments thatvary over time, standard approaches for adjustment of con-founding are biased when there exist time-dependent con-founders that are also affected by previous treatment. Thispaper introduces marginal structural models, a new class of

causal models that allow for improved adjustment of con-founding in those situations. The parameters of a marginalstructural model can be consistently estimated using a newclass of estimators, the inverse-probability-of-treatmentweighted estimators. (Epidemiology 2000;11:550560)

Keywords: causality, counterfactuals, epidemiologic methods, longitudinal data, structural models, confounding, intermediatevariables

Marginal structural models (MSMs) are a new class ofcausal models for the estimation, from observationaldata, of the causal effect of a time-dependent exposure inthe presence of time-dependent covariates that may besimultaneously confounders and intermediate vari-ables.13 The parameters of a MSM can be consistentlyestimated using a new class of estimators: the inverse-probability-of-treatment weighted (IPTW) estimators.MSMs are an alternative to structural nested models(SNMs), the parameters of which are estimated throughthe method of g-estimation.4 6

The usual approach to the estimation of the effect of atime-varying exposure or treatment has been to model the

probability of disease as a function of past exposure and pastconfounder history, using analytic methods such as strati-fied analysis and its parametric analogs (for example, logis-tic or proportional hazards regression). We will show insections 4 and 7.1 that these standard approaches may bebiased, whether or not one further adjusts for past con-founder history in the analysis, when (1) there exists atime-dependent covariate that is a risk factor for, or pre-dictor of, the event of interest and also predicts subsequentexposure, and (2) past exposure history predicts subsequentlevel of the covariate. We refer to covariates satisfyingcondition 1 as time-dependent confounders. Conditions 1and 2 will be true in many observational studies, particu-

larly those in which there is confounding by indication. For

example, in a study of the effect of zidovudine (AZT)treatment on mortality among human immunodeficiencyvirus (HIV)-infected subjects, the time-dependent covari-ate CD4 lymphocyte count is both an independent predic-tor of survival and initiation of therapy with AZT and isitself influenced by prior AZT treatment. In a study of theeffect of obesity on mortality, the development of clinicalcardiac or respiratory disease is an independent predictor ofboth mortality and subsequent weight loss and is influencedby prior weight gain. Conditions 1 and 2 will always holdwhen there are time-dependent covariates that are simul-taneously confounders and intermediate variables. A moredetailed description of the bias of standard methods, as well

as several additional epidemiologic examples of time-de-pendent confounding, has been presented elsewhere.5,7

1. Time-Dependent ConfoundingConsider a follow-up study of HIV-infected patients. Let

Akbe the dose of the treatment or exposure of interest,say AZT, on thekth day since start of follow-up. LetYbea dichotomous outcome of interest (for example, Y 1if HIV RNA is not detectable in the blood and is 0otherwise) measured at end of follow-up on day K 1.Our goal is to estimate the causal effect of the time-dependent treatment Ak on the outcome Y.

Figure 1 is a causal graph that represents our study with

K 1. A causal graph is a directed acyclic graph in whichthe vertices (nodes) of the graph represent variables andthe directed edges (arrows) represent direct causal effects.8

In Figure 1,Lkrepresents the value on day k of the vectorof all measured risk factors for the outcome, such as age,CD4 lymphocyte count, white blood count (WBC), he-matocrit, diagnosis of acquired immunodeficiency syn-drome (AIDS), and the presence or absence of varioussymptoms or opportunistic infections such as oral candidi-asis. Similarly, Uk represents the value on day k of allunmeasured causal risk factors forY. Figure 1,b, differs from

From the Departments of 1Epidemiology and 2Biostatistics, Harvard School ofPublic Health, Boston, MA.

Address correspondence to: James M. Robins, Department of Epidemiology,Harvard School of Public Health, 677 Huntington Avenue, Boston, MA 02115.

This research was supported by NIH grant R01-A132475.

Submitted August 4, 1999; final version accepted February 28, 2000.

Copyright 2000 by Lippincott Williams & Wilkins, Inc.

550


2/11

Figure 1, a, only in that the arrows from the unmeasuredcausal risk factors into the treatment variables have beenremoved. When, as in Figure 1, b, there is no arrow from

unmeasured causal risk factors into treatment variables, wesay that there are no unmeasured confounders given dataon the measured confoundersLk.

9,10 Figure 1,c, differs fromFigure 1, a and b, in that none of the risk factors for Y(measured or unmeasured) has arrows into any treatmentvariable. Note, however, that earlier treatment A0 cancausally affect later treatmentA1. When, as in Figure 1,c,there is no arrow from any (nontreatment) risk factor intoany treatment variable, there is no confounding by eithermeasured or unmeasured factors, in which case we say thattreatment is unconfounded.9,10

The distinctions drawn above apply equally to morefamiliar point-treatment studies in which the treatmentis not time-dependent. As indicated in Figure 2, a point-treatment study is a special case of the general set-up inwhich K 0. Figure 2, ac, contains the analogs ofFigure 1, ac, for a point-treatment study.

As in any observational study, we cannot determinefrom the observed data on the Lk, Ak, and Y whetherthere is confounding by unmeasured risk factors. We canonly hope that whatever residual confounding there maybe due to the Ukis small. Under the untestable assump-tion that there is no unmeasured confounding given theLk, we can, however, empirically test from the datawhether treatment is unconfounded. Specifically, a suf-ficient condition for treatment to be unconfounded isthat, at each time k, among subjects with the same past

treatment history A0, . . ., Ak1, the treatment Ak is

unassociated with the past history of measured covari-ates L0, . . ., Lk.

911 For example, in our point-treatmentstudy, treatment will be unconfounded ifA0 is unasso-ciated with L0.

2. Counterfactuals in Point-Treatment StudiesWe begin with a review of how one would estimate theeffect ofA0on Y in the point-treatment study of Figure2. Suppose treatmentA0is dichotomous; suppose furtherthat Figure 2, c, is the true causal graph, that is, thatneither measured nor unmeasured covariates confoundthe relation between treatment and the outcome. Thenthe crude risk difference, risk ratio, and odds ratio eachmeasure the causal effect of the treatment A0 on theoutcomeY, although on different scales. The crude riskdifference is cRD pr[Y 1A0 1] pr[Y 1A0 0], the crude risk ratio is cRR pr[Y

1A0 1]/pr[Y 1A0 0], the crude odds ratio is

FIGURE 1. Causal graphs for a time-dependent exposure.

FIGURE 2. Causal graphs for a point exposure A0.

Epidemiology September 2000, Vol. 11 No. 5 MARGINAL STRUCTURAL MODELS AND CAUSAL INFERENCE 551


3/11

cOR pr[Y 1A0 1]pr[Y 0A0 0]/{pr[Y 1A0 0]pr[Y 0A0 1]}, and, for example,

pr[Y 1A0 1] is the probability that Y 1 amongtreated subjects (A0 1). We assume that the studysubjects are a random sample from a large, possiblyhypothetical, source population. Probabilities refer to

proportions in the source population.The causal contrasts that correspond to these associa-

tional parameters involve counterfactual variables. Spe-cifically, the variableYa01denotes a subjects outcome iftreated and Ya00 denote a subjects outcome if left un-treated. For a given subject, the causal effect of treat-ment, measured on a difference scale, is Ya01 Ya00.For no subject are both Ya00 and Ya01 observed. If asubject is treated (A0 1), the subjects observedoutcomeYequalsYa01, andYa00is unobserved. IfA0 0,YequalsYa

00, andYa

01is unobserved. Letpr(Ya

01

1) andpr(Ya00 1), respectively, be the probability thatYa01 is equal to 1 and Ya00 is equal to 1. Then, if

treatmentA0is unconfounded, the crude RD equals thecausal risk differencepr[Ya01 1] pr[Ya00 1] in thesource population. The causal risk difference is the aver-age of the individual causal risk differences Ya01 Ya00.Similarly, the crude RR equals the causal RR, pr(Ya01 1)/pr(Ya00 1), and the crude OR equals thecausal OR, pr(Ya01 1)pr(Ya00 0)/{pr(Ya01 0)pr(Ya

00 1)}. Because of the possibility of effect

modification, the population causal parameter neednot equal the causal parameter within a stratum of themeasured risk factorsL0even if treatment is unconfounded.Effect modification is considered in section 9.

3. Models for Point-Treatment StudiesThe causal RD, RR, and OR can also be expressed interms of the parameters of the following linear, loglinear, and linear logistic models for the two counterfac-tual probabilities pr(Ya01 1) and pr(Ya00 1).

pr Ya0 1 0 1a0 (1)

log p rYa0 1 0 1a0 (2)

logit prYa0 1 0 1a0 (3)

where Ya0 is Ya01 ifa0 1 and Ya0 is Ya00 ifa0 0.Specifically, the causal RD

1

, the causal RR e1, and the causal OR e1. Models 13 are saturatedMSMs. They aremarginalmodels, because they model themarginal distribution of the counterfactual random vari-ablesYa01andYa00rather than the joint distribution (thatis, models 13 do not model the correlation ofYa01 andYa00). They arestructuralmodels, because they model theprobabilities of counterfactual variables and in the econo-metric and social science literature models for counterfac-tual variables are often referred to as structural.8,12 Finally,they are saturated, because each has two unknown param-eters and thus each model places no restriction on thepossible values of the two unknown probabilitiespr(Ya01 1) and pr(Ya00 1). Note that these models do not

include covariates, because they are, by definition, models

for causal effects on the entire source population; they arenot models for observed associations.

The crude RD, RR, and OR can also be expressed interms of the parameters of the following saturated linear,log linear, and linear logistic models for the observed out-come Y.

pr Y 1A0 a0 0 1 a 0 (4)

log p rY 1A0 a0 0 1a 0 (5)

logit prY 1A0 a0 0 1 a 0 . (6)

These are models for associations observed when com-paring subpopulations (defined by levels of treatment) ofthe source population. The crude RD equals 1, thecrude RR equals e1, and the crude OR equals e1. Theparameters of the associational models 46 will differfrom the parameters of the MSMs 13, except whentreatment is unconfounded. Because models 4 6 are

models for the observed data, (asymptotically) unbiasedestimates of the model parameters can be obtained usingstandard statistical software (assuming no selection biasor measurement error). When treatment is uncon-founded, these same estimates will also be unbiased forthe corresponding causal parameters of models 13. Forexample, to fit models 46, one could use the general-purpose SAS program Proc Genmod, using the modelstatement Y A0 with the outcome Y specified as abinomial variable. To estimate1, one would specify theidentity link; to estimate1, the log link; and for 1, thelogitlink. Programs analogous to Proc Genmod also existin other packages, such as S-Plus, Gauss, and Stata.1316

4. No Unmeasured ConfoundersSuppose now that treatment is confounded. Then thecrude association parameter will not equal the corre-sponding causal parameter. Similarly, the parameters ofthe MSMs will fail to equal the parameters of the cor-responding observed data models (for example, 0 0and 1 1). Assuming we have no unmeasured con-founders given data on measured confounders L0, unbi-ased estimates of the causal parameters 1, 1, and 1can, however, still be obtained using Proc Genmod byperforming a weighted analysis. Specifically, using theweight statement (that is, option SCWGT) in Proc

Genmod, each subjecti is assigned a weight wi equal tothe inverse of the conditional probability of receivinghis or her own treatment. That is, wi 1/pr[A0 a0iL0 l0i], where, for example,l0iis the observed valueof the variable L0 for subject i. The true weights w i areunknown but can be estimated from the data in a pre-liminary logistic regression ofA0on L0. For example, wemight specify the logistic regression model

logit prA0 1L0 l0 0 1l0 (7)

where A0 is AZT treatment, L0 is, for example, thecolumn vector of covariates with components age, CD4count, WBC count, hematocrit, and presence of symp-

toms, and 1is a row vector of unknown parameters. We

552 Robinset al Epidemiology September 2000, Vol. 11 No. 5


4/11

can then obtain estimates (0, 1) o f (0, 1) usingstandard logistic regression software. Then, for a subjecti with A0 0 and L0 l0i, we would estimate wi 1/pr[A0 0L0 l0i] by 1/{1/[1 exp(0 1l0i)]}1 exp(0 1l0i). For a subject with A0 1 andL0 l0

i

, we would estimatewi 1/pr[A0 1L0 l0i]by {1 exp(0 1l0i)}/exp(0 1l0i) 1 exp( 0 1l0i).

In summary, if there are no unmeasured confoundersgiven data on L0, one can control confounding (due toL0) by modifying the crude analysis by weighting eachsubjecti by w i. The denominator ofwi is informally theprobability that a subject had his or her own observedtreatment. Thus, we refer to these weighted estimators asIPTW estimators.

Why does this approach work? The effect of weightingin Proc Genmod is to create a pseudopopulation con-sisting of wi copies of each subject i. That is, if, for agiven subject,wi 4, the subject contributes four copies

of him- or herself to the pseudopopulation. This newpseudopopulation has the following two important prop-erties. First, in the pseudopopulation, unlike the actualpopulation,A0is unconfounded by the measured covari-ates L0. Second, pr(Ya01 1) and pr(Ya00 1) in thepseudopopulation are the same as in the true studypopulation so that the causal RD, RR, and OR are thesame in both populations. Hence, it follows that we canunbiasedly estimate the causal RD, RR, and OR by astandard crude analysis in the pseudopopulation. Butthis is exactly what our IPTW estimator does, becausethe weights wi serve to create, as required, wi copies ofeach subject. In the Appendix, we present a detailed

numerical example to clarify further our IPTW method-ology, and we compare our methodology with the pro-pensity score methodology of Rosenbaum and Rubin.17

5. Unmeasured ConfoundingIn the presence of unmeasured confounding factors U0,one could still unbiasedly estimate the causal risk differ-ence, risk ratio, and odds ratio as above if one usedweights wi 1/pr[A0 a0iL0 l0i, U0 u0i] inimplementing the analysis in Proc Genmod. Neverthe-less, because data on U0 are not observed, it is notpossible to estimate these weights unbiasedly. Indeed,unbiased estimation by any method is impossible in the

presence of unmeasured confounding factors withoutstrong additional assumptions.

6. Multilevel Treatment and Unsaturated MSMsSuppose again that treatment is unconfounded (as repre-sented in Figure 2, c) but now A0 is an ordinal variablerepresenting a subjects daily dose in units of 100 mg ofAZT. Possible values ofA0are 0, 1, . . ., 14, 15. In that case,the number of potential outcomes associated with eachsubject will be 16. Specifically, we letYa0 be the value ofYthat would have been observed had the subject receiveddosea0rather than the observed dose. Thus, in principle, asubject has a separate counterfactual variable for each of

the 16 possible AZT doses a0. The subjects observed out-

come Y is the outcome Ya0 corresponding to the dose a0equal to the subjects observed dose. For expositional con-venience, we continue to refer to all of the Ya0s as coun-terfactuals, even though fora0equal to the observed dose,Ya0 is the factual variable Y. Because there are so manypotential outcome variables Ya

0

, we can no longer conve-

niently perform a saturated analysis. Rather, we wouldusually assume a parsimonious dose-response relationshipby specifying a linear logistic MSM such as

logit prYao 1 0 1a0 . (8)

This model says that the probability of success had allsubjects been treated with dose a0 is a linear logisticfunction of the dose with slope parameter 1 and inter-cept 0, so e

1 is the causal OR associated with anincrease in AZT dose of 100 mg.

We contrast the MSM model 8 with the followinglinear logistic association model for the observed data.

logit prY

1A0

a0

0

1a0 . (9)Assuming no selection bias or measurement error, we canunbiasedly estimate the associational parameters0and1by fitting the linear logistic model 9 using a standardlogistic regression software package such as SAS Proc Lo-gistic or Proc Genmod. If the treatment is unconfounded,then the parameters of models 8 and 9 are equal. As aconsequence, our logistic regression estimate of1is also anunbiased estimate of our causal parameter 1.

If treatment is confounded by the measured variablesL0, then 1 1 and our standard logistic regressionestimate of1 is a biased estimate of the causal param-eter 1 owing to confounding by L0. However, even

when treatment is confounded, if there are no unmea-sured confounders given L0, then one can obtain unbi-ased estimates of the causal parameter1of model 8 byfitting the logistic model 9 with Proc Genmod if oneuses subject-specific weights w i 1/pr(A0 a0iL0 l0i). Again, in practice, wi is unknown and one mustestimate it from the data by specifying a model.

For example, one might specify the following polyto-mous logistic model:

prA0 a0L0 l0

exp0a0 1l0/

1

j 1

15

exp0j 1l0

,

a0 1, . . . , 15;

prA0 0L0 l0 1/1 j 1

15

exp0j 1l0 (10)which can be fit in SAS using Proc Logistic or Genmodto obtain estimates of the parameters 01, 02, . . ., 015,and 1.

6.1. STABILIZED WEIGHTS

The probabilitiespr[A0 a0iL0 l0i] may vary greatly

between subjects when components of L0 are strongly



5/11

associated with A0. This variability can result in ex-tremely large values of the weightw i for a few subjects.These few subjects will contribute a very large number ofcopies of themselves to the pseudopopulation and thuswill dominate the weighted analysis, with the result thatour IPTW estimator will have a large variance and will

fail to be approximately normally distributed. If theMSM model is saturated (for example, models 13), thisvariability is unavoidable, because it reflects a lack ofinformation in the data as a result of the confounders L0being highly correlated with treatmentA0. For unsatur-ated MSMs, such as model 8, however, this variabilitycan, to a considerable extent, be mitigated by replacingthe weightwi by the stabilized weight swi pr[A0 a0i]/pr[A0 a0iL0 L0i]. To understand the stabilizedweight, supposeA0was unconfounded so that A0and L0are unassociated andpr[A0 a0i] pr[A0 a0iL0 l0i]. Thenswi 1, and each subject contributes the sameweight. WhenA0is confounded,swiwill not be constant

but will vary around the number 1, depending on thesubjects value ofL0. swi, however, will still tend to bemuch less variable thanwi. Furthermore, Robins

1,2 showsthat, when we use the weightswirather than the weightwiin Proc Genmod, the estimates of the parameters ofan MSM remain unbiased and, in the case of an unsat-urated MSM, will generally be less variable. For satu-rated MSMs, the variability of our estimate of will bethe same whether we use the stabilized or unstabilizedweights.

Of course,pr[A0 a0i] andpr[A0 a0iL0 l0i] areunknown and must be estimated. pr[A0 a0iL0 l0i]can be estimated as described above; pr[A0 a0i] can be

estimated as the proportion of subjects in the studysample with A0 equal to a0i. This estimate is equivalentto that obtained by fitting the polytomous model

prA0 a0 exp*0a0/ 1 j 1

15

exp*0j ,a0 1, . . . , 15

prA0 0 1/ 1 j 1

15

exp*0j (11)where we place an asterisk on the parameter *0a0 toindicate that this parameter will differ from the param-eter 0a0 of model 10 when A0 is confounded.

In Ref 2, Robins introduces augmented IPTW estima-tors. These estimators are even more efficient than theIPTW estimator that uses stabilized weights but are moredifficult to compute.

6.2. CONTINUOUS TREATMENTSuppose we were able to measure a subjects daily intakeof AZT to the nearest tenth of a milligram, so that nowAZT is essentially a continuous treatment. Further, forexpositional convenience, assume that no subject has

AZT dose near 0, and that we can effectively model the

distribution ofA0as normal. Now each individual has anextremely large number of counterfactual outcomesYa

0.

One can still obtain unbiased estimates of the causalparameter 1 of model 8 by fitting the logistic model 9with Proc Genmod if one uses the stabilized weightsswi f(a0i)/f(a0il0 i), where f(a0l0) is the conditionaldensity of the continuous variable A0givenL0, andf(a0)is the marginal density of the continuous variable A0. Toestimate f(a0l0), one might specify that, given L0, A0 isnormal with mean 0 1L0 and variance

2. Thenunbiased estimates (0, 1,

2) of (0, 1, 2) can be

obtained by ordinary least-squares regression ofA0on L0using, for example, Proc REG in SAS. Then f(a0il0i)would be estimated by the normal density (2 2)1/2

exp{ [a0i (0 1l0i)]2/2 2}. To estimate the numer-

atorf(a0i) of the stabilized weight swi, one might specifythatA0is normal with mean *0and variance *

2. f(a0i)could be estimated by the normal density (2 *2)1/2

exp[ (a0i *0)2/2 *2] where *0 is the average of the

observedA0s and *2 is their empirical variance. WhenA0 is continuous, estimates based on the unstabilizedweights w i 1/f(a0il0i) have infinite variance and thuscannot be used.1,2

6.3. CONFIDENCE INTERVALS

As described above, we shall estimate the parameters ofthe MSM 8 by fitting the association model 9 in ProcGenmod using estimates of the stabilized weights swi. Ifwe choose the option repeated and specify an inde-pendence working correlation matrix, the Proc Genmodprogram will also output a 95% robust Wald confi-dence interval for 1 given by 1 1.96var(1),

where var(1) is the so-called robust18 or sandwichestimator of the variance of1. Robins

1,2 shows that therobust Wald interval will have coverage probability ofat least 95%, although narrower valid intervals can beobtained with some additional programming.1,2 The or-dinary nonrobust model-based Wald confidence intervaloutputted by most weighted logistic regression programswill not be guaranteed to provide at least 95% coverageand thus should be avoided. Other software packagessuch as S-Plus, Gauss, and STATA also offer robustvariance estimators and could be used in place of ProcGenmod.13,1921

7. Time-Dependent TreatmentsWe now return to the setting of section 1, in which Akis the dose of treatment AZT on thekth day from start offollow-up and Y is a dichotomous outcome variablemeasured at end of follow-up on day K 1. Similarly,Lk represents the value on day k of the vector of allmeasured risk factors for the outcome. LetAk (A0,A1,. . ., Ak) be the treatment or exposure history throughdayk and letA AK. DefineLkand Lsimilarly. LetYabe the value ofYthat would have been observed had allsubjects received dose historya (a0,a1, . . .,aK) ratherthan their observed dose historyA. Note that, even ifakis dichotomous on each day k (that is, on each day a

subject is either on or off treatment), there will be 2K



6/11

dose histories a and thus 2K possible counterfactuals,only one of which is observed (that is, is factual). Thus,it may not be possible to estimate a saturated MSM.Therefore, we would generally assume some sort of par-simonious dose-response relationship by specifying a lin-ear logistic MSM such as

logit prYa 1 0 1cuma (12)

wherecum(a) k 0K akis the cumulative dose through

end-of-follow-up associated with the dose history a.We contrast the MSM 12 with the following linear

logistic association model for the observed data:

logit prY 1A a 0 1cuma. (13)

Assuming no loss to follow-up selection bias or measure-ment error, we can unbiasedly estimate the parameters1by fitting the linear logistic model 13 using a standardlogistic regression software package. If the treatment is

unconfounded, the parameters of models 12 and 13 areequal. As a consequence, our logistic regression estimateof1is also an unbiased estimate of our causal parameter1. If the treatment is confounded, then 1 1and ourstandard logistic regression estimate of 1 is a biasedestimate of the causal parameter 1 as a result of con-founding by Lk. When treatment is confounded, how-ever, if there is no unmeasured confounder given the Lk,then one can still obtain unbiased estimates of the causalparameter 1of model 12 by fitting the logistic model 13with the stabilized weights

sw i k 0

K

pr Ak akiAk 1 a

(k1)i/

k 0

K

prAk akiAk 1 a(k1)i , Lk lki (14)wherek0

K bk b0 b1 b2 . . . bKand A 1is defined to be 0. Note in the special case in whichK 0 (that is, a point-treatment study), models 12 and13 reduce to our previous models 8 and 9 and 14 reducesto our previousswi. The denominator ofswiis informallythe conditional probability that a subject had his or herown observed treatment history through time K. Withtime-dependent treatments the variation in the unsta-bilized weights will often be enormous, with the resultthat the resulting estimator of can be highly variablewith a markedly non-normal sampling distribution. Wetherefore strongly recommend the use of stabilizedweights.

We emphasize that when treatment is confounded, itis the parameter 1 of our MSM 12, as opposed to theparameter 1of the association model 13 that is of policyimportance. To see why, consider a new subject from thesource or target population exchangeable with the Nstudy subjects. We would like to administer to the sub-ject the treatment a that minimized probability that he

or she has detectable HIV in the serum at the end of

follow-up, that is, pr(Ya1). Thus, for example, if theparameter 1 of MSM 12 is positive (that is, the prob-ability of having HIV in the blood increases with in-creasing duration of AZT treatment), we would with-hold AZT treatment from our subject. In contrast, theparameter 1 of model 13 may be confounded by the

association of covariates with treatment. For example,suppose physicians preferentially started AZT on sub-jects who, as indicated by their prognostic factor history(for example, CD4 count), were doing poorly. Further,suppose that AZT had no causal effect on Y (that is,1 0). Then the parameter 1(and thus our estimatefrom the unweighted logistic regression) will be positivebut will have no causal interpretation as the effect ofAZT on Y.

7.1. BIAS INDUCED BY CONTROLLING FOR A VARIABLE

AFFECTED BYTREATMENT

One might suppose that an alternative approach tocontrolling confounding by measured covariates is anunweighted logistic model that adjusts for confounderhistoryL LK, such as

logit prY 1A a, L l 0 1cu ma

2cu m l 3lk 4lk1 5l0

where, for simplicity, we here assume Lk consists of asingle covariate CD4 count at time k. Nevertheless,even under our assumption of no unmeasured confound-ers, the parameter 1differs from the parameter 1of our

MSM. What is worse is that the parameter 1 willgenerally not have a causal interpretation, even if themodel forpr[Y 1A a,L l] is correctly specified.This is because cum(A) depends on a subjects entiretreatment history, including A0, and A0 may affect thetime-dependent covariatesLkand Lk1. Fitting a logisticmodel that adjusts for a covariate that is both affected bytreatment and is a risk factor for the outcome providesan unbiased estimate of the association parameter 1buta biased estimate of the causal parameter 1. This is trueeven under the null hypothesis of no direct, indirect, oroverall treatment effect (so that 1of model 12 equals 0)when, as in Figure 1, a component ofLk (for example,red blood count) and the outcome Y have an unmea-sured common causeU0(for example, the baseline num-ber of bone marrow stem cells).5,7,2226

To summarize, standard regression methods adjust forcovariates by including them in the model as regressors.These standard methods may fail to adjust appropriatelyfor confounding due to measured confounders Lk whentreatment is time varying, because (1) Lk may be aconfounder for later treatment and thus must be adjustedfor, but (2) may also be affected by earlier treatment andthus should not be adjusted for by standard methods. Asolution to this conundrum is to adjust for the time-dependent covariates Lk by using them to calculate theweightsswirather than by adding theLkto the regression

model as regressors.



7/11

8. Estimation of the WeightsWe now describe how to estimate the weights swi. Forsimplicity, we again assume that the treatment Ak ateach time k is dichotomous. Consider first the denomi-nator of model 14. We begin by estimating the unknownprobabilitypr[A

k

1Ak

1Ak1

ak1

,Lk

lk

] usinga pooled logistic model that treats each person-day as anobservation. For example, we might fit the model

logit prAk 1Ak1 ak1 , Lk lk

0 1k 2ak1 3ak2 4lk 5lk1

6ak1lk 7l0 (15)

where, for example,lkis the vector of CD4 count, WBC,hematocrit, and an indicator for symptoms at timek, andthe 4, 5, 6, and 7 are row vectors. This model saysthat the probability of being treated on day k depends ina linear logistic fashion on the dayk, the previous 2 days

treatment, the current and previous days covariates, aninteraction between yesterdays treatments and todayscovariates, and the baseline covariates.

One can fit model 15 using any standard logisticregression program. The numerator probabilities can beestimated similarly, except that, in fitting model 15, weremove the last four terms that are functions of thecovariates. That is, we fit the model as follows:

logit prAk 1Ak1 ak1 *0 *1k *2ak1

*3ak2 . (16)

For each subjecti, we then have our logistic program

output the estimated predicted values p0i, . . ., pKi fromthe fit of model 15, which are maximum likelihoodestimates ofpr[Ak 1Ak1 a(k1)i,Lk lki]. Similarly,we have outputted the predicted valuesp*1i, . . ., p*Kifrommodel 16, which are estimates of the quantitiespr[Ak1Ak1 a(k1)i]. Then we estimate sw i by

sw i k 0

K

p*kiaki1 p*ki

1 aki/

k

0

K

pki )aki(1pki

1 aki

. (17)

For example, 1 p*ki is an estimate of the probabilitypr[Ak akiAk1 a(k1)i] whenaki 0. The data analystwill need to write a small program to compute swi foreach subject from the predicted values outputted fromthe fit of models such as 15 and 16.

Under our assumption of no unmeasured confounders,the resulting estimate of the causal parameter 1will beunbiased, provided the model 15 for pr[Ak 1Ak1 ak1, Lk lk] is correctly specified. Furthermore, underthese same conditions, the 95% robust Wald confidenceinterval will be guaranteed to cover 1 at least 95% ofthe time. The estimate of1will remain unbiased even

if the model 16 for pr[Ak 1Ak1 ak1] is misspeci-

fied.1,2 Indeed, if model 15 is correct and treatment isconfounded, model 16 is guaranteed to be somewhatmisspecified because of the noncollapsibility of logisticmodels.25

9. Effect Modification by PretreatmentCovariatesMSMs can be generalized to allow one to include pre-treatment covariates. For example, model 12 could begeneralized to

logit prYa 1V v 0 1cu ma 2v

3cumav (18)

where V is a component of the vector of measuredpretreatment covariatesL0, and 3denotes a treatment-covariate interaction. Note in model 18, 1 3vrepresents the effect of cumulative treatment on a linear

logistic scale within levelvof the baseline variableV. Asour IPTW estimators already automatically adjust forany confounding due to V, the particular subset VofL0that an investigator chooses to include in model 18should only reflect the investigators substantive inter-est. For example, a variable V should be included inmodel 18 only if the investigator both believes that Vmay be an effect modifier and has greater substantiveinterest in the causal effect of treatment within levels ofthe covariate V than in the source population as awhole.

We obtain unbiased estimates of the parameters ofmodel 18 under the assumption of no unmeasured con-

founders by fitting an association model such as

logit prY 1A a, V v 0 1cuma 2v

3cumav (19)

using Proc Genmod with the estimated weights swiof Eq17, modified only in that p*k is now the estimated pre-dicted value from the fit of a model such as

logit prAk 1Ak1 ak1 , V v *0 *1k

*2ak1 *3ak2 *4v.

Elementary epidemiologic textbooks emphasize that ef-fect modification is logically distinct from confounding.

Nonetheless, many students have difficulty understand-ing the distinction, because the same statistical methods(stratification and regression adjustments) are used bothfor confounder control and detection of effect modifica-tion. Thus, there may be some advantage to teachingelementary epidemiologic methods using marginal struc-tural models, because then methods for confounder con-trol (inverse-probability-of-treatment weighting) aredistinct from methods for detection of effect modifica-tion (adding treatment covariate interaction terms to anMSM).

Finally, an important caveat: MSMs cannot be used

to model the interaction of treatment with a time-



8/11

varying covariate. For this, structural nested modelsshould be used.4 6 Therefore, it is not valid to includein the covariateVin model 18 any components of thetime-dependent covariate Lk measured at any timek 0.

10. Censoring by Loss to Follow-UpHeretofore, we have assumed that each study subjectis observed until end of follow-up at time K 1. Inthis section, we allow for censoring by loss to follow-up. Specifically, let Ck 1 if a subject was lost tofollow-up by day k and Ck 0 otherwise. We assumethat once a subject is lost to follow-up, the subjectdoes not later re-enter follow-up. No new idea isrequired to account for censoring, provided we con-ceptualize censoring as just another time-varyingtreatment. From this point of view, to want to adjustfor censoring is only to say that our interest is in thecausal effect of the treatmentA if, contrary to fact, allsubjects had remained uncensored, rather than havingfollowed their observed censoring history. Our goalremains to estimate the parameter 1 of the logisticMSM 12 except now Ya refers to a subjects outcomeif, possibly contrary to fact, the subject has followedtreatment history a and has never been censored.Again, we can do so if there are no unmeasuredconfounders for both treatment and censoring. Toformalize this idea, one adds at each time k the vari-ableCkto the graph in Figure 1 just beforeLkand after

Ak1. Then, the assumption of no unmeasured con-founders for treatment and censoring is that no arrowarising from the unmeasured causal risk factors U goes

directly into eitherCkor Akfor anyk. In that case, themeasured covariatesLkare sufficient to adjust both forconfounding and selection bias due to loss to follow-up.

Again, we can obtain unbiased estimates of the causalparameters 1 by fitting the linear logistic associationmodel 13 with appropriate weights included. Becausethe outcomeYis unobserved unless the subject does notdrop out, that is,C (C0, . . .,CK1) 0, our weightedlogistic regression fit of model 13 is restricted to uncen-sored subjects. The required subject-specific weight isswi sw i

, where

sw i

k 0

K 1

pr Ck 0Ck1 0, Ak1 a(k1)i/

k 0

K 1

pr Ck 0Ck1 0, Ak1 a(k1)i , Lk lkiand, in addition, in defining and estimating swi, we nowadd to the right side of each conditioning event inmodels 1416 the event Ck 0, because otherwise, Akwould not be observed. The unknown probabilities inswi

can be estimated using a pooled logistic model thattreats each person-day as an observation. Specifically,

we fit analogs of models 15 and 16 for logit pr[Ck

0Ck1 0, Ak1 ak1, Lk lk] and for logit pr[Ck 0Ck1 0, Ak1 ak1]. Note that the denominator ofthe product swi swi

is informally the conditionalprobability that an uncensored subject had his or herobserved treatment and censoring history through timeK 1. Thus, we refer to our weighted logistic estimator

as an inverse-probability-of-treatment-and-censoringweighted estimator. If we view (Ak, Ck) as a jointtreatment at timek, then one can informally interpretthis denominator as simply the probability that a subjectfollows his or her own treatment history, which is ex-actly the interpretation that we had previously in theabsence of censoring.

11. Limitations of Marginal Structural ModelsIt is shown in Ref 2 and Appendix 2 that our IPTWestimators will be biased and thus MSMs should not beused in studies in which at each time k there is a

covariate levellksuch that all subjects with that level ofthe covariate are certain to receive the identical treat-ment ak. For example, this circumstance implies thatMSMs should not be used in occupational cohort stud-ies. To see why, consider an occupational cohort studyin which Ak is the level of exposure to an industrialchemical at timek and Lk 1 if a subject is off work attimekandLk 0 otherwise. Then all subjects with Lk 1 have Ak 0, because all subjects off work are unex-posed. Similarly, in a study of the effect of screening onmortality from cervical cancer, women who have hadtheir cervix operatively removed by time k (which wedenote by Lk 0) cannot receive exposure (that is,screening) at that time, so MSMs should not be used.

Nevertheless, g-estimation of structural nested modelscan always be used to estimate exposure effects, even instudies in which MSMs cannot be used. In many studies,such as the analysis of the Multicenter AIDS CohortStudy data described in our companion paper,27 we be-lieve, based on substantive considerations, the abovedifficulty does not occur and MSMs are a practicalmethod.

12. ConclusionWe have described how to use MSMs to estimate thecausal effect of a time-varying exposure or treatment on

a dichotomous outcome. In our companion paper,27

weextend our results to survival time outcomes and com-pare and contrast methods based on MSMs to alterna-tive, previously proposed methods, based on g-estima-tion of structural nested models and on estimation of theg-computation algorithm formula.

References

1. Robins JM. Marginal structural models. In: 1997 Proceedings of the Sectionon Bayesian Statistical Science, Alexandria, VA: American Statistical As-sociation, 1998;110.

2. Robins JM. Marginal structural models versus structural nested models astools for causal inference. In: Halloran E, Berry D, eds. Statistical Models inEpidemiology: The Environment and Clinical Trials. New York: Springer-

Verlag, 1999;95134.



9/11

3. Robins JM. Correction for non-compliance in equivalence trials. Stat Med1998;17:269302.

4. Robins JM. Structural nested failure time models. In: Andersen PK, KeidingN, section eds. Survival Analysis. In: Armitage P, Colton T, eds. TheEncyclopedia of Biostatistics. Chichester, UK: John Wiley and Sons, 1998;43724389.

5. Robins JM, Blevins D, Ritter G, Wulfsohn M. G-estimation of the effect ofprophylaxis therapy for Pneumocystis carinii pneumonia on the survival of

AIDS patients (erratum in Epidemiology 1993;3:189). Epidemiology 1992;3:319336.

6. Witteman JCM, DAgostino RB, Stijnen T, Kannel WB, Cobb JC, deRidder MAJ, Hofman A, Robins JM. G-estimation of causal effects: isolatedsystolic hypertension and cardiovascular death in the Framingham HeartStudy. Am J Epidemiol 1998;148:390401.

7. Robins JM. A graphical approach to the identification and estimation ofcausal parameters in mortality studies with sustained exposure periods.J Chron Dis 1987;40(suppl 2):139S161S.

8. Pearl J. Causal diagrams for empirical research. Biometrika 1995;82:669688.

9. Pearl J, Robins JM. Probabilistic evaluation of sequential plans from causalmodels with hidden variables. In: Uncertainty in Artificial Intelligence:Proceedings of the Eleventh Conference on Artificial Intelligence. SanFrancisco: Morgan Kaufmann, 1995;444 453.

10. Greenland S, Pearl J, Robins JM. Causal diagrams for epidemiologic re-search. Epidemiology 1999;10:3748.

11. Robins JM. A new approach to causal inference in mortality studies with

sustained exposure periods: application to control of the healthy workersurvivor effect (erratum appear in Math Modelling 1987;14:917921).Mathematical Modelling 1987;7:13931512.

12. Robins JM. The analysis of randomized and non-randomized AIDS treat-ment trials using a new approach to causal inference in longitudinal studies.In: Sechrest L, Freeman H, Mulley A, eds. Health Services Research Meth-odology: A Focus on AIDS. Rockville, MD: National Center for HealthServices Research, U.S. Public Health Service, 1989;113159.

13. SAS Institute Inc. SAS/STAT Users Guide Version 8. Cary, NC: SASInstitute, 1999.

14. S-PLUS 4 Guide to Statistics. Seattle: Mathsoft, 1997.15. GAUSS. Maple Valley, WA: Aptech Systems, 1996.16. Stata. Stata Statistical Software: Release 6.0. College Station, TX: Stata

Corporation, 1999.17. Rosenbaum PR, Rubin DB. The central role of the propensity score in

observational studies for causal effects. Biometrika 1983;70:4155.18. Huber PJ. The behavior of maximum likelihood estimates under non-

standard conditions. In: Proceedings of the Fifth Berkeley Symposium in

Mathematical Statistics and Probability. Berkeley: University of CaliforniaPress, 1967;221233.

19. Carey VJ. YAGS 1.5.1.5: GEE solver for S-plus. In http:/ /biosun1.harvard.edu/carey/index.ssoft.html, 1998.

20. Kallen A. Generalized estimating equations: marginal methods for theanalysis of correlated data. In: Riemann Library. http://www.aptech.com,1999.

21. Stata Corp. Obtaining robust variance estimates. In: Stata Statistical Soft-ware: Release 5.0 Users Guide. College Station, TX: Stata Corporation,1997;235239.

22. Rosenbaum PR. The consequences of adjustment for a concomitant variablethat has been affected by treatment. J R Stat Soc 1984;147:656666.

23. Greenland S, Neutra RR. An analysis of detection bias and proposedcorrections in the study of estrogens and endometrial cancer. J Chron Dis1981;34:433438.

24. Greenland S, Neutra RR. Control of confounding in the assessment ofmedical technology. Int J Epidemiol 1981;9:361367.

25. Greenland S. Interpretation and choice of effect measures in epidemiologic

analyses. Am J Epidemiol 1987;125:761768.26. Robins JM, Greenland S, Hu F-C. Estimation of the causal effect of a

time-varying exposure on the marginal mean of a repeated binary outcome.J Am Stat Assoc 1999;94:687700.

27. Hernan MA, Brumback B, Robins JM. Marginal structural models to esti-mate the causal effect of zidovudine on the survival of HIV-positive men.Epidemiology 2000;11:561570.

28. Horvitz DG, Thompson DJ. A generalization of sampling without replace-ment from a finite universe. J Am Stat Assoc 1952;47:663685.

29. Rosenbaum PR. Model-based direct adjustment. J Am Stat Assoc 1987;82:387394.

30. Robins JM, Rotnitzky A. Recovery of information and adjustment fordependent censoring using surrogate markers. In: Jewell N, Dietz K, FarewellV, eds. AIDS Epidemiology: Methodological Issues. Boston: Birkhauser,1992, pp 2433.

31. Robins JM. Information recovery and bias adjustment in proportional haz-ards regression analysis of randomized trials using surrogate markers. In:Proceedings of the American Statistical Association, Biopharmaceutical

Section, 1993;2433.

Appendix 1: ExampleWe will analyze the data in Table A1 under the assump-tion of no unmeasured confounders given L0. For con-venience, we shall ignore sampling variability and thusthe distinction between parameters of the source popu-lation and their empirical estimates. Under the assump-tion of no unmeasured confounder, pr(Ya01 1) is aweighted average of the L0-stratum-specific risks amongthe treated with weights proportional to the distributionofL0in the entire study population. That is, pr(Ya011) is given by

l0

prY 1A0 1, L0 l0pr L0 l0

(A1)

where the sum is over the possible values of L0.17 We

refer to Eq. A1 as theL0-standardized risk in the treated.Calculating from Table A1, we obtain that pr(Ya01 1) 0.32. Similarly,pr(Ya

0

0 1) is theL0-standardizedrisk in the untreated,

l0

prY 1A0 0, L0 l0pr L0 l0

which, from Table A1, is 0.64. It follows that the causalrisk difference, risk ratio, and odds ratio are 0.32, 0.50,and 0.26. Note that these differ from the crude param-eters computed from Table A2. Thus,1 0.32,1 log 0.50, and 1 log 0.26 in models 13 differ from theparameters 1 0.40, 1 log .044, and 1 log 0.18of models 46.

As is well known, the causal risk difference and causalrisk ratio are also equal to weighted averages of the

stratum-specific risk differences and risk ratios. For ex-ample, the causal RD equals the standardized risk differ-ence (SRD) where

SR D l0

RD l0prL0 l0

and RDl0 pr[Y 1A0 1, L0 l0] pr[Y

1A0 0, L0 l0] is the risk difference in stratum l0.

TABLE A1. Observed Data from a Point-TreatmentStudy with Dichotomous Treatment A0, Stratified by theConfounderL0

L0 1 L0 0

A0 1 A0 0 A0 1 A0 0

Y 1 108 24 20 40Y 0 252 16 30 10Total 360 40 50 50

TABLE A2. Crude Data from the Point-Treatment Studyof Table A1

A0 1 A0 0

Y 1 128 64Y 0 282 26Total 410 90



10/11

Indeed, the usual way to estimate the causal RD is tocalculate the SRD. Our IPTW method is an alternativeapproach to estimation of the causal RDthat, in contrastto the approach based on calculating the SRD, appro-priately generalizes to unsaturated MSMs in longitudinal

studies with time-varying treatments, as discussed insection 7.Table A3 displays the data from the study in a differ-

ent format. In particular, it gives the number of subjectswith each of the possible combinations ofl0,a0, andy, aswell as the weight w 1/pr[A0 a0L0 l0] associ-ated with each. The final column of the table representsthe number of subjects in the weighted pseudopopula-tion for each combination of (l0, a0, y). Note that theweightsw i need not be whole numbers or sum to 1. Asa consequence, the number of subjects in the pseudopo-pulation can be greater than the number in the actualpopulation. Tables A4 and A5 display the data from thepseudopopulation in the same format as Tables A1 andA2. It can be seen thatL0andA0are unassociated in thepseudopopulation, which implies that the treatment isunconfounded. Furthermore, the lack of association be-tween L0 and A0 implies that in the pseudopopulation,the L0-standardized risk in the treated equals the cruderiskpr(Y 1A0 1) 0.32 and theL0-standardizedrisk in the untreated equals the crude risk pr(Y

1A0 0) 0.64. Furthermore, the crude risk in thetreated pseudopopulation equals theL0-standardized riskin the treated actual population and thus equals

pr(Ya01 1). Similarly, the crude risk in the untreatedpseudopopulation equals the L0-standardized risk in the

untreated true population and thus equalspr(Ya00 1).It follows that, under the assumption of no unmeasuredconfounder givenL0, the crude risk difference, risk ratio,and odds ratio in the pseudopopulation equal the causalrisk difference, risk ratio, and odds ratio in the actualpopulation. Finally, an IPTW analysis in Proc Genmodestimates a crude parameter of the pseudopopulation andthus a causal parameter of the actual population.

RELATION TOPROPENSITY SCORE AND HORVITZ-THOMPSON METHODSRosenbaum and Rubin17 refer to the probability pi

pr[A0

1L0

l0i] that subject i would receive treat-ment as the propensity score. Note that IPTW weightwiis not simply the inverse of the propensity score. Spe-cifically, although wi is the inverse of the propensityscore for treated subjects, it is the inverse of 1 pi foruntreated subjects. Rosenbaum and Rubin17 showedthat, under the assumption of no unmeasured confound-ers, one can control for confounding due to measuredcovariates in a point-treatment study with a dichoto-mous treatment by regarding the propensity score as thesole confounder. Because the propensity score pi is acontinuous covariate, however, they suggested that, inpractice, one either approximately match treated withuntreated subjects on the propensity score or stratify(that is, subclassify) on the basis of propensity scorequintiles. Even when there are no unmeasured con-founders and the propensity score is unbiasedly esti-mated, Rosenbaum and Rubins17 approach, unlike ourapproach, suffers from the potential for substantial re-sidual confounding due to the inability to obtain suffi-ciently close matches or to uncontrolled intrastratumconfounding. More importantly, Rosenbaum and Ru-bins17 propensity score methods, in contrast to ourIPTW methods, do not generalize straightforwardly tostudies with nondichotomous or time-dependent treat-ments or exposures.

In the special case of a dichotomous time-indepen-

dent treatment, our IPTW estimator is essentially equiv-

TABLE A3. Inverse Probability of Treatment Weightsw and Composition of the Pseudopopulation in a Point-TreatmentStudy

L0 A0 Y

NObserved

Population pr (A0L0) wN PseudoPopulation

1 1 1 108 0.9 1.11 1201 1 0 252 0.9 1.11 2801 0 1 24 0.1 10 2401 0 0 16 0.1 10 1600 1 1 20 0.5 2 400 1 0 30 0.5 2 600 0 1 40 0.5 2 800 0 0 10 0.5 2 20

TABLE A4. Pseudopopulation Created by Inverse Proba-bility of Treatment Weighting from a Point-Treatment Studywith Dichotomous Treatment A0, Stratified by the Con-founder L0

L0 1 L0 0

A0 1 A0 0 A0 1 A0 0

Y 1 120 240 40 80Y 0 280 160 60 20Total 400 400 100 100

TABLE A5. Crude Data from the Pseudopopulation ofTable A4

A0 1 A0 0

Y 1 160 320Y 0 340 180Total 500 500



11/11

alent to estimating pr(Ya00 1) and pr(Ya01 1)separately among the untreated (a0 0) and treated(a0 1) using the Horvitz-Thompson estimator

28 fromthe sample survey literature.29 Robins and Rotnitzky30

and Robins31 proposed generalizations of the Horvitz-Thompson estimator that could be used to estimate theparameters of a saturated MSM model with a time-varying treatment. Our IPTW estimators are furthergeneralizations that allow the estimation of nonsat-

urated MSMs with both time-independent and time-dependent treatments.

Appendix 2BIAS OF INVERSE-PROBABILITY-OF-TREATMENT WEIGHTEDESTIMATORS IN THE SETTING OF SECTION 11

Consider a new study population for which pr(Ya01 1)and pr(Ya00 1), and therefore the causal risk differ-ence, are the same as for the population in TablesA1A5. The observed data for the new population,however, given in Table A6, differs from the observeddata for the population studied in Tables A1A5. Spe-cifically, Table A6 differs from the observed data inTable A1 only in that no subject with L0 1 receivestreatment A0 1, that is,

pr A0 1L0 1 0, (A2)

and thus represents the type of study discussed in section11. We will show that when Eq A2 holds the IPTWestimator of the causal risk, difference is now biased.

In Table A6, pr(Ya00 1) is again 0.64, the L0-standardized risk in the untreated. Nevertheless, theL0-standardized risk in the treated pr(Y 1A0 1,L0 0)pr(L0 0) pr(Y 1A0 1, L0 1)pr(L0 1) cannot be computed from the data inTable A6, because there is no subject with history(A0 1,L0 1), renderingpr(Y 1A0 1,L0 1) uncomputable. Similarly, the SRDis not computable,because the stratum-specific risk difference is undefinedin the stratum L0 1. Thus, pr(Ya01 1) and thecausal risk difference are not computable from the data

in Table A6, although we know by assumption that theyare still equal to the previous values 0.32 and 0.32.

Table A7 displays the data in Table A6 in the format ofTable A3. Tables A8 and A9 display the stratified andcrude data for the pseudopopulation constructed fromthe last column of Table A7. Note that the SRD inTable A8 for the pseudopopulation is undefined. Thepseudopopulation crude RD from Table A9 is 0.24,which differs from the true causal risk difference 1 0.32. As discussed previously, however, it is the crudeRD in the pseudopopulation that our IPTW estimate ofthe parameter 1 in the MSM pr(Ya0 1) 0 1a0actually estimates. We conclude that our MSM estimateis biased for the causal risk difference 1.

TABLE A6. Observed Data from a Point-TreatmentStudy in Which Eq A2 Holds

L0 1 L0 0

A0 1 A0 0 A0 1 A0 0

Y 1 0 240 20 40Y 0 0 160 30 10Total 0 400 50 50

TABLE A7. Inverse Probability of Treatment Weightswand Composition of the Pseudopopulation in a Point-Treat-ment Study in Which Eq A2 Holds

L0 A0 Y

NObserved

Population pr (A0L0) wN PseudoPopulation

1 1 1 0 0 0*1 1 0 0 0 0*1 0 1 240 1 1 2401 0 0 160 1 1 1600 1 1 20 0.5 2 400 1 0 30 0.5 2 600 0 1 40 0.5 2 800 0 0 10 0.5 2 20

* If N 0 in the observed data, then, regardless of the weight value, there isnobody to be reweighted, so N 0 in the pseudopopulation too.

TABLE A8. Pseudopopulation Created by Inverse Proba-bility of Treatment Weighting from a Point-Treatment Studyin Which Eq A2 Holds

L0 1 L0 0

A0 1 A0 0 A0 1 A0 0

Y 1 0 240 40 80Y 0 0 160 60 20Total 0 400 100 100

TABLE A9. Crude Data from the Pseudopopulation ofTable A8

A0 1 A0 0

Y 1 40 320Y 0 60 180Total 100 500


marginal structural models and causal inference in epidemiolog.pdf

Documents