Control and Instrumental Variables

Causality

• Want to know causal effect of \(X\) on \(Y\)
  • How does education affect wages?
  • How does changing the price you charge affect how much your customers buy?
  • How does sentencing affect crime?

Causal Models

• Data comes from a world where some variables cause other variables
• We describe these relationships by a structural model
  • Potential outcomes, structural equations, or causal graphs
• In some cases, observed data allows us to learn information about (parameters of) causal model
• Last classes: 2 cases where regression can be used to find causal effects
  • Experiments
  • Control
    
• Today
  • When can we use control?
  • What to do when control not possible?

Control: Review

• In situations where control is useful, \(X\) determined by \(W\), with all other variation in \(X\) random (\(Y^x\perp X|W\))
• Causal effect of \(X\) on \(Y\) given by adjustment formula \[E(Y|do(X))=\int E(Y|X,W)P(W)dW\]
• Linear model for \(E[Y|X,W]\) \[Y =\beta_0 +\beta_{1}X +\beta_{2}W + U\]
  • Correct specification of \(E[Y|X,W]\) means \(E[U|X,W]=0\)
    • (Mean) independence of residual
  • \(\beta_1\) gives average treatment effect (ATE) of \(X\)

d-separation in general graphs

• Want rules for arbitrary graphs describing when control is sufficient to recover causal effect
  • First, define rule describing what conditioning implies for independence
• When does conditioning on set of nodes \(W\) imply for two disjoint sets of nodes \(X\) \(Y\) that \(X\perp Y|W\)?
• We say a (non-directed) path from \(X_i\) to \(Y_j\) is blocked by \(W\) if it contains either
  • A collider which is not in \(W\) and of which \(W\) is not a descendant
  • A non-collider which is in \(W\)
• We say \(X\) and \(Y\) are d-separated (by \(W\)) if all paths between \(X\) and \(Y\) are blocked
• Theorem (Pearl, 2009)
  • \(X\perp Y|W\) if and only if \(X\) and \(Y\) are d-separated by \(W\)

Backdoor Criterion

• Using d-separation, can define a complete criterion for when control recovers \(P(Y|do(X=x))\)
• A set of variables \(W\) satisfies Backdoor Criterion between \(X\) and \(Y\) if
  • No node in \(W\) is a descendant of \(X\)
  • \(W\) blocks every path between \(X\) and \(Y\) that contains an edge directed into \(X\)
• Theorem (Pearl, 2009): If \(W\) satisfies the backdoor criterion between \(X\) and \(Y\), the adjustment formula recovers the causal effect of \(X\) on \(Y\) \[P(Y|do(X=x))=\int Pr(Y|W,X=x)Pr(W)dw\]

Backdoor criterion, intuition (Code)

library(dagitty) #Library to create and analyze causal graphs
library(ggdag) #library to plot causal graphs

#Check if W satisfies criterion
isAdjustmentSet(graphname,"W",exposure="X",outcome="Y")
#Find variables that satisfy criterion, if they exist
adjustmentSets(graphname,exposure="X",outcome="Y") 

Backdoor criterion, intuition

• Blocking path component ensures that adjustment variables account for confounding by causes other than the cause of interest and do not introduce additional bias by inducing new correlations through colliders
• Non-descendant component avoids “bad controls” which are themselves affected by treatment
• I will not force you to recall exact definition of d-separation or backdoor criterion
• Point is that given a causal story, systematic method can recover whether control is sufficient
  • In dagitty, check backdoor criterion between \(X\) and \(Y\) by

#Check if W satisfies criterion
isAdjustmentSet(graphname,"W",exposure="X",outcome="Y")
#Find variables that satisfy criterion, if they exist
adjustmentSets(graphname,exposure="X",outcome="Y") 

Example: finding adjustment sets (Code)

complicatedgraph<-dagify(Y~A+C,B~X+Y,A~X,X~C,D~B) #create graph
#Set position of nodes 
coords<-list(x=c(X = 0, A = 1, B = 1, C=1, Y=2, D=2),
     y=c(X = 0, A = 0.1, B=0, C=-0.1, Y = 0, D=0.1)) 
coords_df<-coords2df(coords)
coordinates(complicatedgraph)<-coords2list(coords_df)

#Plot causal graph  
ggdag(complicatedgraph)+theme_dag_blank()
  +labs(title="Complicated Graph") 

Example: finding adjustment sets

Measuring effect of X on Y

• Go back to education \(X\) versus wages \(Y\) to get intuition
• \(A\) caused by \(X\), causes \(Y\): e.g., occupation, experience
  • Mediators: descendant of \(X\), so do not adjust for it
• \(B\) caused by both \(X\) and \(Y\): e.g., current wealth or lifestyle
  • Colliders: descendant of \(X\), so do not adjust for it
• \(D\) caused by \(B\) only: e.g. consequences of wealth
  • Descendants of collider: still causes bias when adjusted for
• \(C\), causes \(X\) and \(Y\): e.g. ability, background
  • Confounder: must condition on it
• Backdoor criterion calculates this automatically

adjustmentSets(complicatedgraph,exposure="X",outcome="Y")

##  { C }

Imperfect control (Code)

confoundgraph<-dagify(Y~X+W,X~W) #create graph
#Set position of nodes 
coords<-list(x=c(X = 0, W = 1, Y = 2),
          y=c(X = 0, W = -0.1, Y = 0)) 
coords_df<-coords2df(coords)
coordinates(confoundgraph)<-coords2list(coords_df)
#Plot causal graph
ggdag(confoundgraph)+theme_dag_blank() 

Imperfect control

• When backdoor criterion fails, OLS will not generally give valid estimates of causal effect
• Why not?
  • May have unobserved causal factors influencing both Y and X
• Can see this in confounding setting
• Can recover ATE by estimating \[Y =\beta_0 +\beta_{1}X +\beta_{2}W + U\] \[E[U|X,W]=0\]

Imperfect Control, ctd

• Suppose we don’t include \(W\)
  • Maybe we just forgot about it
  • Maybe it’s not something we can get data about
• If we omit \(W\), regression becomes \[Y= \beta_0+\beta_1X +\epsilon\] \[\epsilon = \beta_2W+U\]
• Result is \(Cov(X,\epsilon)\neq 0\)
• Estimate of \(\beta_1\) is biased: omitted variables bias

Endogeneity

• General case where OLS gives inconsistent estimate of parameters \[Y=\mathbf{x}^\prime\beta + u\] \[E[\mathbf{x}u]\neq 0 \]
• This is saying OLS assumption (4’) \(E[\mathbf{x}u] = 0\) violated for linear model with causal coefficients
• Here \(\beta\) contains true structural parameter of interest
  • \(u\) NOT just difference between \(Y\) and best linear predictor of \(Y\)
• Omitted variables are common cause of endogeneity
• OLS estimate not consistent for \(\beta\)

An alternative: Instrumental variables (IV)

• Consider a simple regression with endogeneity \[Y=\beta_0+\beta_1X + u\] \[E[Xu]\neq 0 \]
• We don’t have controls to add to regression to solve this
• We might have some variables \(Z\) that don’t matter for \(Y\), or at least not directly
• In particular, \(Z\) affects \(X\) but not \(Y\)
• All influence of \(Z\) on \(Y\) comes via effect on \(X\)
  • None through whatever is in \(u\)
• Then we may be able to find effect of \(X\) by looking only at variation in \(X\) which is coming through \(Z\)

Goal of IV estimation

• \(Z\) is randomly assigned, but \(X\) isn’t
• AND \(Z\) only has direct effect on \(X\), not \(Y\)
  • The “Part of \(X\) determined by \(Z\)” is then effectively random
• Example: Effect of going to a particular school \(X\) on wages \(Y\)
• Admission to school determined by lottery \(Z\)
• Not all admitted students attend: some go to other schools
  • Reasons determined by unobserved personal characteristics \(W\)
• \(X\) not random, due to missing controls
• \(Z\) is random, uncorrelated with \(W\)
• We could get effect of \(Z\) on \(Y\), but really want effect of \(X\)
• IV lets us use the randomness of \(Z\) to estimate effect of \(X\)

Causal graph of IV model (Code)

ivgraph<-dagify(Y~X+W,X~W, X~Z) #create graph
#Set position of nodes 
coords<-list(x=c(X = 0, W = 1, Y = 2, Z=-1),
          y=c(X = 0, W = 0.1, Y = 0, Z=0)) 
coords_df<-coords2df(coords)
coordinates(ivgraph)<-coords2list(coords_df)
#Plot causal graph
ggdag(ivgraph)+theme_dag_blank()
  +labs(title="Instrumental Variables") 

Causal graph of IV model

• No arrows into \(Z\)
  • Determined independently
• Arrow from \(Z\) to \(X\), but not to \(Y\)
  • Z has direct effect on X but not on Y
• If \(W\) were observed, could use control to find effect of \(X\) on \(Y\)
• If \(W\) not observed, but \(Z\) is, can use instrumental variables estimator

Finding an instrument

• Instruments offen the result of a natural experiment
• \(X\) maybe determined by many things,
  • But one of them acts effectively like an experiment
• Something like a random number generator somehow influences \(X\), among other influences
• Maybe this is an actual random number generator
  • E.g. a lottery, or a coin flip
• We don’t care about effect of coin flip itself on outcome
  • Want to use it estimate effect of \(X\)
• E.g., Admission lottery for school allows us to estimate effect of Enrollment on outcome (like wages)
  • Even if enrollment not random
  • Determined in part by unobserved preference for school
  • Lottery has no direct effect on wages, but does affect enrollment

Estimation in IV Model

• Let \(\beta_1\) be true causal effect. Then regression equation \[Y=\beta_0+\beta_1X + u\] has \[E[Xu]\neq 0 \]

• \(X\) is called the endogenous regressor
• We have another variable \(Z\) called the instrument

• It satisfies 2 conditions: Exogeneity and Relevance

• Exogeneity: \[Cov(Z,u)=0\]

• Relevance: \[Cov(Z,X)\neq 0\]

• Let’s see how these let us solve the endogeneity problem

• Then go back to see what they mean

One more assumption

• Model \[Y=\beta_0+\beta_1X + u\]
• Add 1 more assumption \[E[u]=0\]
• Assumption is weak
  • Can always change \(\beta_0\) to equal \(\beta_0+E[u]\) if not true
  • If we don’t care about \(\beta_0\), this is not a problem
  • IV will still let us estimate \(\beta_1\)

Finding \(\beta_1\) using IV

• Model \[Y=\beta_0+\beta_1X + u\]
• Exogeneity \[Cov(Z,u)=0\]
• Relevance \[Cov(Z,X)\neq 0\]
• Mean 0 errors \[E[u]=0\]

Finding \(\beta_1\)

• Rewrite Assumptions using model
• Mean 0 errors \[E[Y-\beta_0-\beta_1X]=0\]
• Exogeneity \[Cov(Z,u)=E[Zu]-E[Z]E[u]=E[Zu]=0\]
• This becomes \[E[Z(Y-\beta_0-\beta_1X)]=0\]
• System of 2 linear equations in 2 unknowns

Solving the system

\[E[Y-\beta_0-\beta_1X]=0\] \[E[Z(Y-\beta_0-\beta_1X)]=0\]

• This becomes \[\beta_0=E[Y]-\beta_1E[X]\]

• Plug in to second equation \[E[Z((Y-E[Y])-\beta_1(X-E[X]))]=0\] \[\beta_1=\frac{E[Z(Y-E[Y])]}{E[Z(X-E[X])]}\] \[\beta_1=\frac{Cov(Z,Y)}{Cov(Z,X)}\]

IV Estimator

• We just identified the parameter in terms of features of observable distribution \[\beta_1=\frac{Cov(Z,Y)}{Cov(Z,X)}\] \[\beta_0=E[Y]-\beta_1E[X]\]
• Suppose we have random sample of n draws of \((X_i,Y_i,Z_i)\)
• We can estimate by replacing expectations with sample averages

\[\hat{\beta}_1^{IV}=\frac{\frac{1}{n}\sum_{i=1}^{n}(Z_i-\bar{Z})(Y_i-\bar{Y})}{\frac{1}{n}\sum_{i=1}^{n}(Z_i-\bar{Z})(X_i-\bar{X})}\] \[\hat{\beta}_0^{IV}=\frac{1}{n}\sum_{i=1}^{n}Y_i-\hat{\beta}_1^{IV}\frac{1}{n}\sum_{i=1}^{n}X_i\]

Relevance Condition

• We assumed relevance: \(Cov(Z,X)\neq 0\)
• Need this for estimator to have a solution, to define \[\beta_1=\frac{Cov(Z,Y)}{Cov(Z,X)}\]
• In words, instrument needs to be correlated with endogenous regressor
• This allows us to use \(Z\) say something about effect of \(X\)

Exclusion restriction

• We assumed exogeneity of \(Z\): \(E[Zu]=0\)
• Sometimes this is called Exclusion Restriction
• In words, \(Z\) cannot be correlated with the residual
  • Even though, by assumption, \(X\) is
• Usually because \(Z\) has no direct causal effect on \(Y\)
• In case of omitted variable bias, means \(Z\) is uncorrelated with omitted variable
• Note difference from strategy of control:
  • To control, we want to find the omitted variable and include it
  • For IV, want something totally unrelated to omitted variable
• Idea: want to find a source of variation in \(X\) which is effectively random, even if \(X\) in general is determined nonrandomly

Reduced Form and First Stage

• Total effect of \(Z\) on \(Y\) consistently estimable by regression
• Regression of \(Y\) on \(Z\) called reduced form
  • Slope is \(\rho = Cov(Y,Z)/Var(Z)\)
  • By exclusion restriction, we know this only comes indirectly, through instrument’s effect on \(X\)
• Effect of \(Z\) on \(X\) consistently estimable by regression
  • Regression of \(X\) on \(Z\) called first stage
  • Slope is \(\pi = Cov(X,Z)/Var(Z)\)
• IV is \[\beta_1=Cov(Y,Z)/Cov(X,Z)= \rho/\pi\]

IV interpretation

• IV adjusts reduced form (quasi)experimental estimate of effect of instrument \(Z\) on outcome \(Y\) by amount experimental treatment actually affected \(X\)
• Consider 2 cases

1. First stage \(\pi\) small, but total effect \(\rho\) of instrument on outcome big
   • Then effect must have come from very large effect of \(X\)
   • \(X\) didn’t move much even though outcome did
2. First stage \(\pi\) big but total effect \(\rho\) of instrument on outcome small
   • \(X\) must have small effect
   • \(X\) moved a lot with the experiment but outcome \(Y\) mostly stayed the same

Example: Effect of longer prison sentences on recidivism

• Example drawn from [Green and Winik (2010, Criminology)]
• Policy question: how long should prison sentences be?
  • Incarceration has many potential costs and benefits, need to know what they are to evaluate.
• To measure benefits, need measure of outcomes given longer or shorter sentences
• Outcome variable: \(Y\)
  • Measure of recidivism for people on trial for a particular crime
• Variable of interest \(X\)
  • Length of prison sentence given to offender
• Ideal experiment
  • Randomly assign prison sentences to criminals
  • Measure recidivism and regress on sentence length
• But this hasn’t been done
  • Would be unethical

Endogeneity problem

• Instead, look at prison sentences assigned the usual way
  • A judge using sentencing guidelines and discretion
• Endogeneity problem
  • People assigned longer prison sentences likely differ from those given shorter sentences
  • May be more likely to be guilty,
  • Or have characteristics that make judge think they are
  • Or likely to be at risk of recidivism
• If we could include all variables influencing judge’s decision and find functional form replicating their judgment, could control for them
• This is hard:
  • Decisions include component based on perceive probability of reoffending
  • Likely to be correlated with actual reoffending
• Instead, look for instrument
  • Something affecting sentences which is random

IV solution

• In this case, can use one random component of trials:
  • Judges assigned randomly to defendants
• Z is random judge assignment (say, to judge 1 or judge 2)
• Don’t care about effect of judge 1 vs judge 2 per se
  • Given by reduced form regression of \(Y\) on \(Z\)
• Clear that \(Z\) satisfies exogeneity: \(E[Zu]=0\)
  • Random choice of judge is unrelated to defendant characteristics
• \(Z\) satisfies relevance \(Cov[ZX]\neq0\) if 1 judge tends to give harsher sentences than the other on average for any given defendant
  • Maybe judge 2 interprets sentencing guidelines in different way, or just has different temperament or judgment
• IV finds the difference in recidivism associated with variation in sentence length due to having been randomly assigned a different judge

IV Results

• Green and Winik find IV estimates close to 0
• Mechanically: effect of which judge one assigned to on recidivism rate is extremely small
• Dividing this effect by the difference in sentences due to the difference in judges, which was non-negligible, suggests that different sentences can’t have affected recidivism that much

Conclusions

• Causal graph determines conditional independence relationships
  • Backdoor criterion describes when control strategy can be used to estimate treatment effect
• When proper controls not observed or included, regression coefficients have endogeneity bias
• Might still be able to estimate effect if data contains an instrument
  • An instrument is a variable which leads to variation in a treatment \(X\) without directly affecting the outcome \(Y\)
  • With an instrument, can use instrumental variables estimator to measure treatment effect

Next 2 classes

• More about IV
• Read Ch 15 in Wooldridge
• Read Ch 3 in Angrist and Pischke