NONCOMPLIANCE BIAS CORRECTION BASED ON COVARIATES IN RANDOMIZED EXPERIMENTS

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1 NONCOMPLIANCE BIAS CORRECTION BASED ON COVARIATES IN RANDOMIZED EXPERIMENTS YVES ATCHADE AND LEONARD WANTCHEKON Noveber 1, 2005 Abstract We propose soe practical solutions for causal effects estiation when copliance to assignents is only partial and soe of the standard assuptions do not hold. We follow the potential outcoe approach but in contrast to Ibens and Rubin 1997), we require no prior classification of the copliance behaviour. When noncopliance is not ignorable, it is known that adusting for arbitrary covariates can actually increase the estiation bias. We propose an approach where a covariate is adusted for only when the estiate of the selection bias of the experient as provided by that covariate is consistent with the data and prior inforation on the study. Next, we investigate cases when the overlap assuption does not hold and, on the basis of their covariates, soe units are excluded fro the experient or equivalently, never coply with their assignents. In that context, we show that a consistent estiation of the causal effect of the treatent is possible based on a regression odel estiation of the conditional expectation of the outcoe given the covariates. We illustrate the ethodology with several exaples such as the access to influenza vaccine experient McDonald et al 1992) and the PROGRESA experient Shultz 2004)). Key words: Causal inference, Intent-to-treat, Noncopliance, Randoized experients JEL Classification: C14, C21, C52 Departent of Matheatics and Statistics, University of Ottawa. Departents of Politics and Econoics, New York University. The authors are grateful to Dr McDonald for sharing with us the data fro their study on the effect of influenza vaccination on orbidity. This work is supported in part by the Natural Sciences and Engineering Research Council of Canada. 1

2 1 Introduction Randoized experients are a widely accepted approach to infer causal relations in statistics and social sciences. The idea dates back at least to Neyan 1923) and Fisher 1935) and has been extended by D. Rubin and co-authors Rubin 1974), Rubin 1978), Rosebau and Rubin 1983)) to observational studies and other ore general experiental designs. In this approach, causality is defined in ters of potential outcoes. The causal effect of a treatent, say Treatent 1 copared to another treatent, Treatent 0) on the variable Y and on the statistical unit i is defined as Y i 1) Y i 0) where Y i ) is the value we would observe on unit i if it receives Treatent. The estiation of this effect is probleatic because unit i cannot be given both treatents. This difficulty is circuvented by randoizing the receipt of the treatents. To estiate the causal effect of a treatent, two rando saples of units are selected, the first group is assigned to Treatent 0 and the second group to Treatent 1. The difference in the saple eans of Y or soe statistic of interest) over the two groups is used as an estiate of the causal effect of the treatent. The ain idea is that randoization eliinates at least in theory) any systeatic difference between the two saples. We refer the reader to Holland 1986) for an interesting discussion of causality in statistics. But in practice, it happens often that soe units do not coply with their assignents. On a large scale, noncopliance liits the internal validity of the experient and ay introduce severe bias in the estiation of the causal effect of the experient. A trivial exaple of the effect of noncopliance is one in which a harful drug is adinistered and units assigned to the drug who recover after the experient are erely those who did not coply with their assignent. In general, in presence of noncopliance, the causal effect of the treatent is ore difficult to define and less useful) as it depends on the treatent assigned to. One widely used approach to deal with noncopliance is Intention-to-Treat ITT) analysis see e.g. Lee et al 1991)). ITT proposes precisely to ignore the noncopliance proble and to use the effect of the assignent as a proxy for the treatent effect. In ITT, one sees the noncopliance behaviour as part of the response to the treatent. Therefore, an ITT estiate can be interpreted as the use-effectiveness of the treatent. It is particularly useful when the noncopliance behaviour is believed to be stable over tie. However, the ITT estiates can be strikingly different fro the real treatent effect particularly when noncopliance is severe and/or changes over tie. This could be a proble if the experienter is ainly interested in the real 2

3 effect of the treatent. An alternative to the Intent-to-Treat estiate is the Local Average Treatent Effect LATE) proposed by Angrist et al 1996) see also Ibens and Rubin 1997)). The LATE estiate is the ITT estiate divided by the proportion of units that coply with their assignent. Assuing four patterns of copliance behavior copliers, never-takers, always-takers and defiers), these authors have shown under soe additional assuptions) that the LATE estiate can be given a causal interpretation as the causal effect of the treatent over the sub-population of copliers. The LATE estiate is interesting because copliers are precisely the units for which speaking of the causal effect of the treatent akes sense. But the approach is of a liited applicability since this sub-population of copliers is generally) not known and cannot be defined precisely. Moreover, assuing such a rigid classification of copliance behavior ay liit the external validity of the ethod. In this paper, we take the approach that noncopliance is a rando behavior driven by covariates and that there is no rigid classification of the copliance behavior. In order to define precisely the causal effect of the treatent we ake the so-called exclusion restriction assuption Angrist et al 2002)), assuing that Y t, d) and Y t, d) have the sae distribution for any t, t, d {0, 1}. This aounts to assuing that the assignent has no direct effect on the outcoe but through the received treatent. In this fraework, we ask two questions. Is it possible to consistently estiate the causal effect of the treatent if: 1. the noncopliance behavior is not ignorable given the observed covariate? 2. soe sub-population called in the sequel taboo population ) can never be enticed to take the treatents? Regarding question 1 we show that when noncopliance is not ignorable given the available covariates, controlling for arbitrary covariates can actually worsen the estiation bias. We then propose an approach where prior inforation on the study is cobined with the data to deterine which covariates one should adust for. The idea is based on the fact that adusting for a covariate corrects only for the selection bias of the experient as seen through that covariate that is, after conditioning on that covariate). Therefore adusting for a covariate can increase the bias if the covariate has a wrong picture of the selection bias of the experient. When appropriate inforation is available, it is possible to find how well a covariate will estiate the selection bias of the experient and whether that covariate should be adusted for or not. Question 2 is an exaple where the so-called overlapping assuption breaks down. It is quite frequent in edical studies where units are screened based on their covariates before partici- 3

4 pating in the experients and yet the experienter would like to estiate the causal effect of the treatent over the whole population See also Wantchekon 2003) for a randoized experient in political science where this proble arises 1 ). In this paper, we foralize the selection of the units in this type of experients as a sequence of negative binoial trials and we show that if a global) representation of the conditional expectation of the outcoe given the covariates exists then it can be consistently estiated fro the data and used to estiate the causal treatent over the whole population including the taboo sub-population). By estiating the potential treatent effect on the untreatable units, that is, units that cannot be assigned neither to Treatent 1 nor to Treatent 0, our ethod provides a general and foral test of external validity of randoized experients. This could turn out to be a very useful exercise, especially in edical trials where the experienter is interested estiating the effect of a drug on a sub-population that cannot participate in the experient presuably because of potential side effects of the drug). The rest of the paper is organized as follows. In Section 2, we develop the basic fraework for covariate-based bias correction. This classical aterial is presented here for copleteness. Its presentation also allows us to introduce the estiators that we use next. In Section 3.1, we present our new ethod for bias reduction in the presence of unobserved covariates and in Section 3.2, we show how to consistently estiate the causal treatent effect in presence of a taboo sub-population. We present several exaples to illustrate our ethods in Section 4. We then present a re-analysis of an experient to access the effect of an influenza vaccine conducted by McDonald et al 1992) see also Hirano et al 2000)). 2 Noncopliance bias correction with observed covariates In this section, we present the basic fraework of the potential outcoe odel for causal inference in randoized experients with noncopliance. We include these well known results here to ake it easier for the reader to follow our discussion in Section 3. The basic assuptions are detailed in Section 2.1. Soe consistent estiators of the causal effect are presented in Section Wantchekon 2003) presents results fro an experient in which non-copetitive electoral districts were randoly assigned to purified national public goods and redistributive platfors by candidates copeting in the 2001 presidential elections in Benin. We ay want to estiate the potential causal effect of the treatent if copetitive and ethnically diverse districts have participated in the experient. 4

5 2.1 The basic fraework A rando saple of n units fro a reference population is taken and each unit is assigned to Treatent 1 or Treatent 0. Let T 1,..., T n ) be the rando vector of assignents; T i = if unit i is assigned to Treatent, = 0, 1 and i = 1,..., n. Define the rando variable C i = 1 if unit i coplies with its assignent and 0 if not. Finally define D i to be the treatent actually received by unit i. D i = 1 if unit i actually receives Treatent 1 and D i = 0 it unit i actually receives Treatent 0. If T i = t and D i = d, we observe the outcoe Y i t, d). We assue that Y i t, d) is a rando variable with finite expectation. Let X i be a vector of covariates pretreatent variables) observed on unit i before its assignent to a treatent. We assue that Y i 0, 0), Y i 0, 1), Y i 1, 0), Y i 1, 1), X i ) 1 i n are independent and identically distributed i.i.d.) and when there is no abiguity, we shall oit the subscript i when referring to an arbitrary eleent of the saple. Following Angrist et al 1996) we assue that: Assuption A1): Pr Y i 0, d) X) = Pr Y i 1, d) X), a.s. for d = 0, 1. 1) The idea behind A1) is that the assignent variable T can affect the outcoe variable Y only through the received treatent variable D so that the conditional distribution of Y 0, d) and Y 1, d) given X are the sae for d = 0, 1. We find this assuption quite realistic in ost applications. But it can be questionable in situations where assignent to a given treatent can significantly change the behavior of the subect and therefore have a direct ipact on the outcoe. For d = 0, 1, let µ d x) := E Y 0, d) X = x) = E Y 1, d) X = x) and µ d := E Y 0, d)) = E Y 1, d)) where the second equalities follow fro A1). We are interested in the causal effect of Treatent 1 versus Treatent 0 at covariate level X = x defined as τx) = µ 1 x) µ 0 x), 2) and ost iportantly, the causal effect of the treatent over the population defined as: τ p = µ 1 µ 0. 3) The well-known proble in estiating τx) and τ p is that all the outcoe variables Y i t, d) cannot be observed in the sae tie. Throughout the paper, we assue that the assignent is ignorable given the covariates; we assue that: Assuption A2): Y i 0, 0), Y i 0, 1), Y i 1, 0), Y i 1, 1)) T i X i, 1 i n, 4) 5

6 where for rando obects X, Y the notation X Y eans that X and Y are independent and for rando variables X, Y, Z, we write X Y Z to say that X and Y are conditionally independent given Z. If we have Cov X, Y Z) := E XY Z) E X Z) E Y Z) = 0 we shall say that X and Y are uncorrelated given Z. Siilarly, if CovX, Y ) := EXY ) EX)EY ) = 0, we say that X and Y are uncorrelated. Reark 1 1. Assuption A2) is not restrictive in randoized experients. Often the assignents are actually randoized independently fro any covariate. A2) also includes the case of stratified randoization where the blocks are defined on soe covariate X. 2. One iportant consequence of A1) and A2) is that for all purposes, we can now define the outcoe variable Y without entioning the assignent under which it is observed. More precisely, let Y d) = Y 0, d)1 {T =0} + Y 1, d)1 {T =1}. For d = 0, 1, we have: Pr Y d) A X) = Pr Y 0, d) A T = 0, X) PrT = 0 X) + Pr Y 1, d) A T = 1, X) PrT = 1 X) = Pr Y 0, d) A X) PrT = 0 X) + Pr Y 1, d) A X) PrT = 1 X), by A2)) = Pr Y 0, d) A X) = Pr Y 1, d) A X), by A1)). For the rest of the paper we always assue A1) and A2) and write Y i d) for the outcoe of unit i that receives treatent d without necessarily entioning its assignent. The ost iportant and certainly ost controversial assuptions in randoized experients are the next two assuptions. Assuption A3): Y i 0), Y i 1)) C i T i, X i ), 1 i n, 5) Define ex) = PrD = 1 X = x) as the probability of taking Treatent 1. This function is called the propensity score of the experient. Assuption A4): For any x X, 0 < ex) < 1. 6) 6

7 Assuption A3) asserts that noncopliance is ignorable given the covariate vector X so that it can affect the outcoe Y i) only through X, and A4) is the so-called overlapping assuption that says that every unit have a positive chance of taking both treatents. These assuptions are well-known and are at the heart of ost covariate-based adustents that have been proposed in observational studies see e.g. Rosenbau 2002)). In practice, they are very difficult to check. Most of the tie one has to resort to specific knowledge of the phenoenon under study to udge whether these assuptions are reasonable given the covariates at hand. Our obective in this work is to show, in soe special cases where these assuptions are known not to hold, that it is still possible to liit the bias in estiating the causal effect of the treatent. Assuption A4) also allows us to define E Y d) X, D = d) as E [Y d) X, D = d] := E [ 1 {D=d} Y d) X ]. Pr [D = d X] It can be easily seen that under the assuptions enuerated above, the receipt of treatent is ignorable and that τ P is consistently estiable. Proposition 1 Under A1)-A4), we have: Y d) D X, d {0, 1}. 7) This iplies that E Y d) X, D = d) = E Y d) X) so that τ P data available. is consistently estiable fro the Although Proposition 1 is directly usable to estiate τ P, very often in practice, particularly when the diension of the covariates X is large, it is ore efficient to adust for noncopliance on low-diensional covariates. Rosebau and Rubin 1983) introduced the concept of propensity scores and showed that it has that desired property. Their result in our context is as follows: Proposition 2 Assue A1)-A4). Let b : X Y be a easurable function such that there exist easurable functions g : Y R for which ex) = gbx)), x X. We have: i) ii) X D bx). 8) Y 0), Y 1)) D bx), 9) Moreover if b : X Y is any easurable function that satisfies i) and ii) above then necessarily, ex) = qbx)) for soe easurable function q. 7

8 2.2 Soe practical iplications of Propositions 1 and 2 Here we explore briefly soe practical iplications of Propositions 1 and 2 in estiating τ P in presence of noncopliance. There are any standard ways to adust for covariates in randoized experients that can be used here. We consider the use of the propensity scores and the regression functions. For ore details, and for a review see Ibens 2003) Weighting on propensity scores It is clear fro Proposition 1 that: E [Y d) X] = E [Y d) X, D = d] [ ] 1{D=d} Y d) = E PrD = d X) X. { } { } 1{D=1} Y 1) 1{D=0} Y 0) Therefore τx) = E ex) X E 1 ex) X. If êx) denotes a consistent estiate of e, τ P can be consistently estiated by: ˆτ 1 = 1 n n i=1 1{Di =1} êx i ) 1 ) {D=0} Y i, 10) 1 êx i ) where Y i = 1 {Di =1}Y i 1) + 1 {Di =0}Y i 0) is the outcoe observed on the i-th unit. We can estiate ex) with various paraetric or nonparaetric ethods using the observed value of the variable D, X). In the exaples that we consider below, we use a paraetric logistic regression odel. The estiator 10) is well known in randoized experients. It has been shown by Hirano et al 2003) Theore 1) that under soe regularity conditions, if e 1 and e 0 are consistently estiated, ˆτ 1 is consistent, efficient and asyptotically noral Correction based on the regression function Let µ d x) = E Y d) X). Again fro Proposition 1 we have E ) Y d) X, 1 {D=d} = E Y d) X). Therefore, we can use the observed values on Y, X) on the units that received Treatent d to obtain a consistent estiate ˆµ d x) for µ d x), d = 0, 1. This can be done using various paraetric and nonparaetric regression ethods. Then a consistent estiate for τ is given by: ˆτ 2 = 1 n n ˆµ 1 X i ) ˆµ 0 X i )). 11) i=1 8

9 2.2.3 Subclassification and atching on the propensity scores As peritted by Proposition 2, the propensity score can also be used to generate a new estiator that copares the outcoe variables for siilar levels of the propensity score, which is the so-called sub-classification on the propensity score ethod. Suppose we have an estiate ê of the propensity score e. Let 0 = b 1 < b 2 < b L+1 = 1 be a subdivision of [0, 1] constructed such that the values êx i ) for which êx i ) B l := [b l, b l+1 ] are approxiately equal. For l = 1,..., L, let: n l = be the size of B l, and n 1 Bl êx i )), 12) i=1 ˆτ l) = n i=1 Y id i 1 Bl êx i )) n i=1 D i1 Bl êx i )) n i=1 Y i1 D i )1 Bl êx i )) n i=1 1 D i)1 Bl êx i )). 13) be the estiate of the causal effect for units in B l. Then the subclassification estiator for τ P is given by: ˆτ 3 = L l=1 n l n ˆτ l). 14) The atching ethod see e.g. Ibens 2003) and Diaond and Seckon 2005)) is a special case of subclassification with one treated unit and a fixed nuber M of control units typically M = 1) per B l. Matching is particularly useful when the nuber of control units is uch larger than the nuber of treated units. 3 Inference under violated assuptions 3.1 Effect of unobserved covariates In this section, we no longer assue A3). So it is possible that there is soe unobserved covariate that is linked to the outcoe variable and to the copliance behaviour. As discussed in the introduction, it is particularly difficult to ake valid statistical inference in randoized experients with noncopliance when the noncopliance behaviour is not ignorable. That is when Assuption A3) doesn t hold. When faced with nonignorable noncopliance behaviour, the general approach in practice sees to include as uch covariables as possible in the analysis. But as shown by Spirtes 1997) when iportant covariables are unobserved, it is perfectly possible that controlling for all the observed covariates increases the estiation bias. In other words, unless all the iportant covariates related to the experient are observed, adusting for the observed covariates can actually increase the estiation bias. 9

10 In this work, we argue that in randoized experient with noncopliance, one should be ore caution and select only the covariates that can reproduce roughly well the selection bias of the experient. We start with a theoretical result that will help clarify what we eant in the sentence above. Then we will discuss the details of how to ipleent the approach. Forally, we want to answer two questions. What is the bias incurred if we proceed in estiating the causal effect τ p without the unobserved covariate? Can we expect to reduce that bias copared to the situation where no covariates are controlled for? To siplify the notation, we write e d x) = PrD = d X = x), d = 0, 1, so that e 1 x) = ex) and e 0 x) = 1 ex). Also recall that µ d X) = E Y d) X). Theore 3 Assue A1), A2), A4)and for d = 0, 1, define ε d X) = E [ 1 {D=d} Y d) X ] e d X)µ d X). 15) Then for d = 0, 1, E [ [ ] ] 1{D=d} Y d) Y d) X, 1 {D=d} = E X e d X) = E Y d) X) + ε dx) e d X). 16) A first approxiation of the expectation of the bias ter B d X) := ε dx) e d X) gives: where δ d = PrD = d) 1 [ E [B d X)] δ d [ Cov 1{D=d}, Y d) ) Cov e d X), µ d X)) ], 17) Ee 2 d X)) [Ee d X))] 2 Cov [ ed X) Ee d X)), ε d X) Eε d X))] ]. Proof. Equation 16) is trivial. For rando variables X and Y with a finite second oent, it is easily seen that: X Y EX) EY ) = Taking the expectation yields: [ ] X E Y XEY ) Y EX) EY )) 2 [ 1 + Y EY ) EY ) ] XEY ) Y EX) EY )) 2 EX) EY 2 ) ) Cov X, Y ) EY ) EY )) 2 EX)EY ) 1 Y EY ) ) EY ) Since E e d X)) = PrD = d) and E ε d X)) = Cov 1 {D=d}, Y d) ) Cov e d X), µ d X)), applying the approxiation forula above with X = ε d X) and Y = e d X) gives: [ ] εd X) [ E δ d Cov 1{D=d}, Y d) ) Cov e d X), µ d X)) ], 18) e d X) where δ d is given as above. 10

11 Since A3) doesn t hold, if we use the data fro the experient to estiate µ d X) = EY d X), what we will actually be estiating is E Y d X, 1 {D=d} ). The bias incured is E Yd X, 1 {D=d} ) µ d X) and Theore 3 shows that the expected bias is approxiately E [B d X)] δ d [ Cov 1{D=d}, Y d) ) Cov e d X), µ d X)) ]. Note that Cov 1 {D=d}, Y d) ) / PrD = d) is the overall selection bias due to noncopliance in estiating EY d)). Now, the ter Cov e d X), µ d X)) / PrD = d) can be seen as the estiate provided by the covariate X of that selection bias Cov 1 {D=d}, Y d) ) / PrD = d). Therefore if X provides a correct estiate of the selection bias, that is if if Cov e d X), µ d X)) Cov 1 {D=d}, Y d) ) for d = 0, 1, then adusting on X will reduce the selection bias. But if X is such that Cov e d X), µ d X)) and Cov 1 {D=d}, Y d) ) are very different quantities, it is best not to adust on X as this will increase the estiation bias. When prior inforation exists, this result can be used to screen to set of observed covariates in order to used the ost relevant Covariates selection with prior inforation As discussed above, our selection ethod consists in finding all the covariates X for which Cov e d X), µ d X)) and Cov 1 {D=d}, Y d) ) are roughly equal. Since neither of these quantities can be coputed is ost experient, we settle with a less rigorous rule: select all the covariates for which Cov e d X), µ d X)) and Cov 1 {D=d}, Y d) ) have the sae signs. Although the actual values cannot be estiated, in any cases, it is possible to use prior inforation on the experient to find an estiate of the signs of the quantities. Since Cov 1 {D=d}, Y d) ) / PrD = d) = E Y d) D = d) E Y d)), we need to copare the overall expected outcoe to the expected outcoe of units that choose to receive d. Such inforation is available in any studies. To obtain the sign of Cov e d X), µ d X)), we rely on the following well known result. Let Y be a rando variable and f and g two onoton functions. If f and g has the sae onotonicity then Cov fy ), gy )) 0 otherwise Cov fy ), gy )) 0. In our case, the onotonicity of e d x) can be obtained by estiating that function fro data. The onotonicity of µ d x) = E Y d) X = x) cannot be estiated fro the data in general. But in any studies this inforation can be available. Here is an exaple of how to apply the ethod. Assue that fro prior inforation, we know the sign of E Y d) D = d) E Y d)), d = 0, 1. For exaple, assue that E Y 1) D = 1) E Y 1)) 0 and that E Y 0) D = 0) E Y 0)) 0. Note that this inforation does not say anything about the effect of the treatent but is related instead to what is known about the noncopliance behavior. For exaple, E Y 1) D = 1) E Y 1)) 0 siply says, speaking about 11

12 the outcoe when Treatent 1 is received, that those who choose to receive that treatent happen to have on average) a larger value of the outcoe. Let X be the observed covariate vector and also assue that prior inforation exists which gives us the onotonicity of µ d x). To fix the ideas, assue that µ d x) is nondecreasing for d = 0, 1. Let ê 1 x) be an estiate of e 1 x) obtained fro the data. Our rule to decide whether to control for X is as follows. If we find out that ê 1 x) is nondecreasing in x, then it is likely that Cov e 1 X), µ 1 X)) 0 which is consistent with E Y 1) D = 1) E Y 1)) 0. Siilarly, since µ 0 x) is nondecreasing, we likely have Cov e 0 X), µ 0 X)) 0 which is consistent with E Y 0) D = 0) E Y 0)) 0. Therefore X will be included in our list of potentially useful covariates. But if we find out that ê 1 x) is nonincreasing in x) then X is likely to increase the estiation bias and should not be used. The ethod is repeated for each easured covariate to deterine the final set of covariates to be used to control for the noncopliance bias. We use that ethod to re-analyze a randoized experient with encourageent designed to easure the effect of an influenza vaccine. See Section Inference in taboo population In this section, we deal with situations where it is not actually possible to apply the treatents to the whole population. Assue that there exist thresholds < z t) and continuous functions Z t) : X R t = 0, 1) such that any unit i with covariate X i for which Z t) X i ) > z ) cannot be given Treatent t or equivalently that such unit will never coply with Treatent t). Therefore we have e 1 x) = ex) = 0 for Z 1) x) > z 1) and e 0 x) = 1 ex) = 0 for Z 0) x) > z 0) so that A4) does not hold. We call the sub-populations {x : Z 1) x) > z 1) } and {x : Z 0) x) > z 0) } taboo sub-populations. A coon exaple where this odel arises naturally is in edical studies where units are first screened on soe pre-treatent variables, the so-called eligibility criteria, in order to deterine their participation to the experient. Although only a subset of the whole population can participate to the experient, soeties one is still interested in inferring the causal effect of the treatent on the whole population fro such an experient. We argue here that if a global odel for the treatent effect is plausible then the effect of the treatent over the whole population is estiable. The arguent is very siple and is based on the following seen conditional expectation: [ ] E Y d) X, 1 {Z d) X) z d) } = 1 {Z d) X) z d) } E [Y d) X]. 19) Fro this, it follows that if we have an iid saple Y i d), X i ) where Z d) X i ) z d), using an appropriate regression odel, we can obtain a consistent estiate for E [Y d) X = x] 12

13 on {x : Z d) x) z d) }. If E [Y d) X = x] has a global paraetric for, then the regression analysis will consistently estiate those paraeters and E [Y d) X = x] can then be estiated outside {x : Z d) x) z d) }. That is the basic idea that we are proposing. In practice, because of the sapling schee the way the units are screened and assigned to the treatents), the final saple Y i d), X i ) where Z d) X i ) z d) is generally not iid. There are any ways to design the sapling of the experient. We ention two basic ethods. In one for a fixed nuber of units is screened and randoized to the two ars of the experients and the nubers of units by treatent is finally rando. In the other for, units are screened and randoized to the treatents until a predeterined nuber of units are obtained for both treatents. Here the total nuber of units screened is rando. We assue the latter sapling ethod. That is, we assue that we have an infinite reservoir of units that are screened and assigned until the first tie a given nuber of units, say n 1, is assigned to Treatent 1. For i 1, let Y i 0), Y i 1), X i, T i and Y i 0), Y i 1)) are independent given X i. For t {0, 1}, define τ t) 0 = 0 and for k 1 define τ t) k := inf ) be a sequence of i.i.d. rando variables such that T i { n > τ t) k 1 : T n = t, Z t) X n) z t)}. 20) We assue that ρ t := Pr T 1 = t, Zt) X 1 ) zt)) > 0 so that all these rando ties τ t) k finite. The rando tie τ 0) 1 is the first unit assigned to Treatent 0 that is under the threshold z 0) and thus will receive that treatent. Siilarly, τ 0) k is the k-th unit assigned to Treatent 0 that satisfies the constraint and thus will receive that treatent. Iplicitly, we assue that there is no further noncopliance issue after a unit satisfies the constraint. Siilar explanations hold for the stopping ties τ 1) k. The sapling is stopped after n 1 units have been assigned to Treatent 1. Let be the nuber of units screened before obtaining the n 1 units assigned to Treatent 1. Let n 0 be the nuber of unit assigned to Treatent 0 during the sapling. Here and n 0 are rando. follows a Negative Binoial distribution with paraeters n 1 and ρ 1 and given, n 0 follows a Binoial distribution with paraeters and ρ 0. Recall that for t = 0, 1, ρ t := Pr T 1 = t, Zt) X 1 ) zt)). Finally, we assue that all the covariates X i ) 1 i tested during the sapling are kept in order to copute the causal effect for the entire population. The idea we are about to use is siple. are Although the special sapling used to obtain the two saples induces a dependence between the observations, it actually does not change the dependence between the outcoe and the covariates of any one unit and our arguents above should work as well. To continue, we assue the following global representation of the conditional expectation of Y d) as functions of the covariates: 13

14 Assuption A5): There exist known easurable functions h d) 1,..., hd) p d ) and paraeters β d) = β d) 1,..., βd) p d ) such that E Y d) X = x) = H d β, x) = p d i=1 β d) i h d) i x), d = 0, 1. 21) The additive odel postulated in Assuption A5) is quite flexible. By allowing the user to specify the coponent functions h d) i, that approach akes it easier to use prior knowledge available on the dependence between the outcoe and the covariates. When no such inforation exists, It is always possible to use a ore systeatic set of functions like 1, X 1, X 2,..., X p, X 1 X 2, X 1 X 3..., where here, X i is the i-th coponent of X. Another possible approach is to use a nonparaetric additive odel. In this odel, the regression function is taken as H d β, x) = p d h d) i i=1 hd) i x), where is an unknown function and estiated nonparaetrically, for exaple as in Horowitz and Maen 2004). The iportant point is that A5) is a working assuption and other ore general) global odelling is also possible. Let ˆβ 1) be the Ordinary Least Square OLS) estiate of β 1) in the regression of the outcoe Y on h 1) 1 X),..., h1) p 1 ) X)) obtained fro the saple Y 1) τ, X 1) i τ. Siilarly, define i 1 i n 1 by ˆβ 0) ) the OLS estiate of β 0) coputed fro the saple Y 0) τ, X 0) i τ. We introduce the i 1 i n 0 estiator ˆτ 4 := 1 [ ˆβ1) ) H, X ˆβ0) )] i H, X i. 22) It turns out that: i=1 Theore 4 Assue A1)-A3) and A5). Then, E ˆτ 4 ) τ p as n 1, where τ p is the treatent effect over the whole population. Proof. It suffices to show that E 1 ˆβ1) )) i=1 H, X i EY 1)) as n 1. A siilar arguent will apply for E 1 ˆβ0) )) i=1 H, X i and the Theore will be proved. ) It is not hard to see that E Y, X τ 1) 1,..., X = β 1) h 1) X ), where h 1) x) = i τ 1) i. x),..., h1) p 1 x)) Therefore: h 1) 1 1 ˆβ1) ) ) ) E H, X 1 i = β 1) E h 1) Xi ). 23) i=1 The proof will be finished once we prove that for any 1 p 1, E 1 E h 1) X1 ). ) i=1 ) i=1 h1) Xi ) 14

15 If i is such that T i = 1, and Z 1) Xi ) z1), then: ) E Xi ) = 1 x)l 1 x)µ X dx), ρ 1 h 1) h 1) D 1 where µ X is the distribution of X, D 1 = {x X : Z 1) x) z 1) }, l 1 x) = PrT = 1 X = x). If i is such that T i = 0, and Z 0) Xi ) z0), then: ) E Xi ) = 1 x)l 0 x)µ X dx), ρ 0 h 1) h 1) D 0 where D 0 = {x X : Z 0) x) z 0) }, l 0 x) = 1 l 1 x). And if i is such that T i = 1, and Z 1) X i ) > z1)) or T i = 0, and Z 0) X i ) > z0)), then: E h 1) ) Xi ) = 1 1 ρ 0 ρ 1 where Ā represents the copleent of A. Fro these expressions, we deduce that: ) 1 E h 1) Xi ) = 1 n1 ) E ρ i= n0 ) E ρ 0 ) h 1) x)l 1 x)µ X dx) + h 1) x)l 0 x)µ X dx), D 1 D 0 h 1) D 1 h 1) D E 1 ρ 0 ρ 1 + x)l 1 x)µ X dx) x)l 0 x)µ X dx) n0 ) n1 E )) [ D ] 1. h 1) x)l 0 x)µ X dx) D 0 h 1) x)l 1 x)µ X dx) Given n 0 distributed as a Binoial distribution with paraeters, ρ 0, therefore 1 ρ 0 E n 0 ) = 1. As we saw, is distributed as a Negative Binoial distribution with paraeters n 1 and ρ 1, therefore 1 ρ 1 E n 1 ) 1 as n1. And we get: after soe siplifications. ) 1 E h 1) Xi ) i=1 h 1) x)µ X dx), as n 1 4 Application 4.1 A siulation exaple Here we conduct a Monte Carlo experient to illustrate that Intent-to-Treat and the Local Average Treatent Effect can be seriously biased as estiates of the treatent effect over the 15

16 population. Let X 1, X 2 be two covariates defined on soe population and assue that X 1 N60, 15) and X 2 N2, 0.5). We would like to estiate the causal effect of a treatent Treatent 1) copared to Treatent 0 over that population. We take 2N with N = 850) units and randoly evenly split the over the two treatents such that for any unit i, P T i = 1) = 1/2. We assue that there is full copliance with assignent to Treatent 0; that is, D i = T i if T i = 0. But copliance to Treatent 1 is not perfect. More specifically, we have P C i = 1 T i = 1, X 1 = x 1, X 2 = x 2 ) = exp{α 0 + α 1 x 1 + α 2 x 2 } 1 + exp{α 0 + α 1 x 1 + α 2 x 2 }, with α 0, α 1, α 2 ) = 5,.005, 1). Let Y be the response or outcoe variable. We ake the exclusion-restriction assuption and assue that if a unit receives Treatent, = 0, 1, we observe Y i) and Y i) X 1 = x 1, X 2 = x 2 ) N β i,0 + β i,1 x 1 + β i,2 x 2 + β i,3 x 1 x 2, 1), where β 0,0, β 0,1, β 0,2, β 0,3 ) = 3.8, 0.01, 1, 0.01) and β 1,0, β 1,1, β 1,2, β 1,3 ) = 5, 0.05, 1, 0). The paraeters are chosen such that EY 0)) = 0 and EY 1)) = 0 and therefore the treatent has no effect on the population. As the reader can see, the exaple is constructed in such a way that units with relatively large values of X 1, X 2 ) tend not to coply to assignent to Treatent 1 which appears to be harful for that sub-population. They switch to Treatent 0 which is ore beneficial for the. We copare the ITT estiate and the LATE estiate with ˆτ 1, ˆτ 2 and ˆτ 3. Let Y i be the response observed on the i-th unit. We copute the ITT and LATE estiates as: IT T = 1 2N Y i T i N i=1 2N i=1 Y i 1 T i ) IT T LAT E = 1 2N N i=1 D it i ). 2N i=1 D i1 T i ) We have siulated this odel 250 ties to copute the eans of the various estiates as well as their standard errors. Table 1 shows the results. ), Table 1: Means and standard errors of the causal effect estiates. ITT LATE ˆτ 1 ˆτ 2 ˆτ 3 Mean Std error [0pt] Graph 1: Density estiates for the distribution of the 5 estiators used. insert Graph 1 here) 16

17 It is clear fro this exaple that Intent-to-Treat and the Local Average Treatent Effect are not good estiates of the real treatent over the population. When noncopliance can be fairly well-predicted fro the covariates available, as in this exaple, the estiates proposed in this paper provide better estiates. In case of LATE, that estiate is correct if we restrict our interest to the sub-population of copliers. But as discussed in the introduction, such a sub-population is not well-defined here; thus, the estiate doesn t tell us anything about the real effect of the treatent over the whole population. 4.2 Assessing the effect of an influenza vaccine We reanalyze a randoized experient conducted by McDonald et al 1992) to assess the efficacy of influenza vaccination in reducing flu-related orbidity in high-risk populations. The study has also been reanalyzed by Hirano et al 2000). The study was designed to circuvent the ethical proble of denying the vaccine to part of the population while giving it to others as in a classical randoized experient. Physicians in a public hospital were randoly assigned either to the treatent group or to the control group. When a high-risk patient whose physician is in the treatent group is scheduled for an appointent, a coputer-generated letter is sent to the physician to encourage her to vaccinate the patient. According to the US Public Health Service Criteria, patients over 65 years of age or with chronic lung disease, astha, diabetes ellitus, congestive heart failure or severe renal or hepatic failure are at high-risk of flu. For a given patient i, we observe T i, which is 1 if that person s physician is in the treatent group and a letter is sent to encourage the physician to vaccinate the patient, or 0 otherwise. The patient ay choose to coply with its assignent T i in which case C i = 1 or not, in which case C i = 0. We also observe the variable D i which is 1 if the patient actually receives the flu shot and 0 otherwise. The outcoe variable is a binary variable Y i t, d) which is 1 if the patient i is subsequently aditted in hospital for flu during the next winter, or 0 otherwise. The age age) and various edical condition variables are also observed on the patients before the assignent. These are copd {0, 1} for chronic pulonary disease, 1 is yes ; d {0, 1} for diabetes ellitus, 1 is yes ; heartd {0, 1} for heart disease, 1 is yes ; renal {0, 1} for severe renal failure, 1 for yes ; liverd {0, 1} for chronic hepatic failure, 1 is yes. The gender sex {0, 1}, 1 for ale and race {0, 1}, 1 for Caucasian, 0 for non-caucasian are also given. We ignore these last two variables in our analysis. See table 2, for a suary of the data. [0pt] Table 2: Saple eans for the variables of interest over the subpopulations defined by Z and D. 17

18 Z D Y age copd d heartd liverd sex race Z= Z= D= D= Following Hirano et al 2000), we ignore the clustering of the units through the physicians. We do this to keep the analysis siple and also because we do not have sufficient inforation on the clustering. Therefore we can consider the assignent to the flu shot as copletely randoized so that A2) holds. In contrast to Hirano et al 2000), we ake the exclusion-restriction assuption Assuption A1)) that there is no difference in the distribution of the outcoe between the patients who had a different assignents but received the sae treatent. Given that the study involves ainly seniors ost of the with high risk to influenza, it sees likely that there are all well aware of the threat posed by the flu season and the basic ways to protect theselves. Therefore it is very unlikely that a discussion with their physician will ake a systeatic difference. 2 Finally we assue A3 ) and A4) and use the ethod developed in Section 3.1. It is very plausible and we shall assue that if all the patients were given the flu shot, those who choose voluntarily to take the shot would probably have a higher hospitalization rate: Cov 1 {D=1}, Y 1) ) 0. 24) Siilarly, if all the patients were denied the shot, those who choose not to take the shot would probably have a lower hospitalization rate: Cov 1 {D=0}, Y 0) ) 0. 25) In relation with the covariates, another reasonable hypothesis is that for any covariate vector X {age, copd, d, heartd, renal, liverd}: E Y 0) X) and E Y 1) X) are roughly nondecreasing in X. For exaple it sees reasonable to assue that older patient will have higher hospitalization rate than younger patients. Siilarly, patients suffering fro any above-entioned disease is likely to have a higher hospitalization date than patients not suffering fro that disease. If we agree with the prior inforation on the study, then we could use this inforation to screen the observed covariates to deterine which ones agree and are therefore likely to reduce the noncopliance bias. Table 2 shows PrD = 1 X) varies with X for the different covariates. When X = age, we estiate the PrD = 1 X) using a logistic regression and report the correlation 2 Hirano et al 2000) sees to suggest otherwise. 18

19 between ˆPrD = 1 X) and X. When X is any one of the other binary variable we report the saple estiate of PrD = 1 X = 1) PrD = 1 X = 0). Fro this table, and given the ethod outlined in Section 3.1.1, we are lead to adust for the covariates age, copd, d, heartd, renal. Table 3: Estiate of the onotonicity between PrD = 1 X) and X when X is the different covariates observed. age copd d heartd liverd Based on these assuptions and the final set of selected covariates, we use the estiator ˆτ 2, to estiate the causal effect of the treatent over the population and also over different subset of high risk patients. The results are suarized in Table 3. We copute the treatent effect for the entire population and for different high risk sub-populations. The standard errors are estiated by bootstrapping. Fro these results, we conclude that there is no evidence that the vaccination has any particular effect on the hospitalization rate in general. But for individuals at high risk, our analysis strongly suggests that the vaccination has iproved the hospitalization rate for those high risk groups even though the effects are not statistically significant. Table 4: Overall treatent effect and treatent effect for soe high risk groups overall age> 65 copd d heartd Mean s.d Effect of the Progresa progra In this exaple we analyse the ipact of the Mexican Progresa poverty progra on school attendance for childreen between 13 and 15 years of age. For a detailed description of Progresa, we refer the reader to Schultz 2004). Progresa was a vast utli-year progra ipleented by the Mexican governent to reduce poverty. It has been designed as a randoized experient. The governent has first identify all the localities where poverty was of concern. 495 localities where found. A census was conducted in October 1997 to collect inforation on incoe, consuption, assets etc... on all the households in these localities. The data fro the census was used to deterine a poverty index. Only very poor households with poverty index below a threshold) were elligible for 19

20 Progresa. So the taboo population here is the households with poverty index above that threshold. The households are not directly randoized. The localities are randoly assigned to receive the progra or to serve as control and all the households in that localities are treated accordingly. Out of the 495 poor localities, 314 have been assigned to receive the Progra, the reaining localities serving as control. The Progresa progra itself is ade up of three coponents. There is an educational grant to facilitate and encourage the education of childreen. The progra also gives an iproved health services to all the ebers of the participating household. And a onetary transfer is provided to help satisfy their basic needs. We estiate the effect of the progra on the shool attendance of childreen between 13 and 15 years old, 1 year after the beginning of Progresa. The covariates used in our analysis are based on the 1997 preliinary survey. The experient offers a direct estiate of the effect of the progra on poor childreen childreen in elligible household). It is certainly also of interest to estiate the effect that the progra would have on rich childreen childreen in non-elligible household). Following the approach outlined above, we used a logistic regression odel to estiate the effect of the progra on school attendance in the group of poor childreen. For each of the two ars of the experient, if we assue that the logistic odel is well specified, then the estiated odel also gives a consistent estiate for the regression of school attendance on the covariates for the whole population in that ar of the experient. Therefore a causal effect of Progresa for rich childreen and for the whole population can be infered. The resuts are presented in Table 5. It appears according to these estiates that the effect of the progra for rich childreen would be coparable although slightly less iportant than what has been observed for poor childreen. Table 5: Estiate of Progresa ipact on Mexican population. The estiates for Rich and Overall are the effect, as given by our odel, that we would have observed if Progresa was extended to this group. Poor Rich Overall Mean s.d Conclusion In the paper we have considered randoized experients where soe of the classical assuptions do not hold. Firstly, we have considered randoized experients with noncopliance when the noncopliance is not ignorable. We Instead using all available covariates, a solution 20

21 that ay perfor badly, we have proposed a covariate selection ethod that select the best subset of covariates to adust on in order to iniize the estiation bias. Our ethod requires that soe prior inforation on the experient be available. In the second part of the paper, we have considered experients where an elligility criteria based on soe observed covariate is required to enter the different ars of the experient. Despite the fact that only a subset of the population can enter the experient, we have shown that a nonparaetric odel can be used to estiate the regression function of the treatents effect on the covariates. We have used this odel to estiate the causal effect of the treatent over the whole population. References [1] Angrist, J.D., Ibens, G.W. and Rubin, D. 1996). Identification of causal effects using intruental verbals with discussion), JASA [2] Diaond, A. Seckhon, J.S. 2005). Genetic Matching for estiating causal effects: a new ethod of achieving balance in observational studies. Technical report, Departent of Governent, Harvard University [3] Fisher, R. 1935). The design of experients. Boyd, London [4] Hirano, K., Ibens, G. and Ridder, G. 2003). Efficient estiation of average treatent effects using the estiated propensity score. Econoetrica [5] Hirano, K., Ibens, G.W., Rubin, D.b. and Zhou, X.-H. 2000). Assessing the effect of an influenza vaccine in an encourageent design. Biostatistics [6] Holland, P. 1986). Statistics of causal inference. Journal of Aerican Statistical Association [7] Horowitz, J. L. and Maen, E. Nonparaetric estiation of an additive odel with a link function. Annals of Statistics, 32, [8] Ibens, G. W. 2003). Seiparaetric estiation of average treatent effects under exogeneity: a review, Technical Report, Departent of Econoics, UC Berkeley [9] Ibens, G. W. and Rubin, D. 1997). Bayesian Inference for causal effects in randoized experients with noncopliance. Annals of Statistics

22 [10] Lee, Y. Ellenberg, J. Hirtz, D. and Nelson, K. 1991). Analysis of clinical trials by treatent actually received: is it really en option? Statistics in edicine [11] McDonald, C., Hiu, S., Tierney, W. 1992). Effects of coputer reinders for influenza vaccination on orbidity during influenza epideics MD Coputing [12] Neyan J. 1923). On the application of probability theory to agricultural experients. essay on principles. section 9 with discussion) translated in Statistical Sciences vol 5, No [13] Rosebau, P. 2002). Observational Studies. Springer, New York. [14] Rosebau, P. R. and Rubin, D.1983). The central role propensity score in observational studies for causal effects. Bioetrika [15] Rubin, D. 1974). Estiating causal effects of treatents in randoized and non randoized studies. Journal of Educational Psychology [16] Rubin D. 1978). Bayesian Inference for causal effects: the role of randoization. Annals of statistics [17] Spirtes, P. 1997). Liits on causal inference for statistical data. presented at the Aerican Econoics Association eetings [18] Wantchekon, LO. 2003). Clientelis and voting and behavior: Evidence fro a field experient in Benin World Politics

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