ECON 6074: Causal Inference
Module 3 - Year 2022/2023
Topic 5. Instrumental Variable 1
Last Lecture - Matching
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Matching is another way to eliminate selection bias by controlling
observable covariates
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This can be accomplished by matching treated and untreated units
with the same characteristics
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Matching is constructing a comparison sample of untreated units
with the same observable characteristics as the sample of treated
units
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Identification relies on the Conditional Independence
Assumption:
I
I
(Yi1 , Yi0 ) ⊥
⊥ Di |Xi
After matching treated and control groups on observed covariates
Xi , treatment assignment is considered as good as random
Example: Effect of MECON program on Monthly Salary
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Want to know treatment effect of MECON on earnings
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Assume that age is the only confounding factor
No.
MECON
Age
Salary
Matched Sample
No.
Age
Salary
No.
Non-MECON
Age
Salary
1
2
3
4
5
29
28
33
34
27
40,000
45,000
42,000
38,000
36,000
7
15
6
10
9
29
28
33
34
27
28,000
35,000
30,000
46,000
26,000
6
7
8
9
10
11
12
13
14
15
33
29
30
27
34
23
30
24
23
28
30,000
28,000
32,000
26,000
46,000
21,000
43,000
29,000
26,000
35,000
Avg
30.2
40,200
Avg
30.2
33,000
Avg
28.1
31,600
Review - Propensity Score Matching
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Instead of matching over K dimensions, the method of propensity
score matching (PSM) allows the matching problem to be reduced
to a single dimension
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The propensity score is defined as the treatment probability
conditional on a set of observed variables Xi :
p(Xi ) = E [Di |Xi ] = Pr(Di = 1|Xi )
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Intuitively, propensity score p(Xi ) summarizes all information of a
set of covariates Xi into a single value
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Then, by controlling the propensity score p(Xi ) we can eliminate
selection bias
Review - Identification with PSM
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Under conditional independence assumption we can identify the
causal effect by controlling for covariates that affect the probability
of treatment
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The propensity score theorem tells us that the only covariate you
need to control for is the probability of treatment itself:
p(Xi ) = Pr(Di = 1|Xi )
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Similar to identification with matching estimator, the only difference
is that we control p(Xi ) instead of a set of covariates
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The key condition for identification (≈ eliminate selection bias) is
E [Yi0 |p(Xi ), Di = 1] = E [Yi0 |p(Xi ), Di = 0]
Today’s Outline
Topic 5. Instrumental Variable
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Identification Results
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Estimation of LATE
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IV in RCT
Instrumental Variable
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The Instrumental Variable (IV) method exploits an exogenous source
of variation that drives the treatment Di but unrelated to other
confounding factors ui that affect outcome Yi
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Intuitively, IV breaks variation of the treatment Di into two parts:
1. Correlated with other confounding factors
2. Uncorrelated with other confounding factors
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We use the variation in Di that is uncorrelated with ui to estimate
the causal effect of treatment
Main Idea of Instrumental Variable
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Y is an outcome (e.g. earnings), Z is the instrument, D is the
treatment (e.g. Masters degree), and u is the unobserved
confounding factor (e.g. ability)
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Ability might be a confounder affecting both Masters degree and
earnings
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More able people are more likely to attain Masters degree
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More able people receive higher earnings
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In this case, we need to find an IV that generates variation in
receiving Masters degree D which is uncorrelated with ability u
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IV is based on a chain of causal reactions
Conditions of Valid IV
To become a valid IV it needs to satisfy the following conditions:
1. Strong first stage (relevance): Z → D
2. Exclusion Restriction (exogeneity):
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No direct or indirect effect of the instrument Z on the outcome Y
through variables other than the treatment variable D
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That is, the instrument Z affects the outcome Y only through the
treatment variable D
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The instrument Z is uncorrelated with confounding factors u
Can we test these conditions?
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We can test whether the instrument has relevance - how?
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However, we cannot test whether the instrument is exogenous - why
not?
Example: Angrist (1990)
Joshua Angrist (1990) “Lifetime Earnings and the Vietnam Era Draft
Lottery: Evidence from Social Security Administrative Records”,
American Economic Review. 80(3): 313-336
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The paper examines the effect of military service on lifetime income
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We will use this paper as an example to go through the key concepts
of IV methods
Angrist (1990) - Empirical Challenge
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Joining military service is a personal choice
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Is there any selection bias due to unobservable confounding factors
in this example?
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Risk preference:
I Risk-loving people may voluntarily join military service
I Risk-loving may have negative impact on lifetime earnings (e.g. risk
preference affects other decisions such as human capital investment,
job search, etc..)
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Health condition:
I More healthy people join military service
I More healthy people also have higher earnings (e.g. more productive,
more workdays, etc..)
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We need to find a valid IV for the treatment variable, joining
military service, that is uncorrelated with confounding factors
Angrist (1990) - Background
Angrist (1990) uses the Vietnam draft lottery (Zi ) as an IV for joining
military service
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In the 1960s and early 1970s, young American men were drafted for
the military service to serve in the Vietnam war
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Concerns about the fairness of the conscription policy led to the
introduction of a draft lottery in 1970
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From 1970-1972, random sequence numbers were assigned to each
birth date in cohorts of 19 year olds
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Men with lottery numbers below a cutoff were elibible for being
drafted while men with numbers above the cutoff was not
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The draft did not perfectly determine military service:
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Many draft-eligible men were exempted for health and academic
reasons
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Draft-ineligible men volunteered for service
Angrist (1990) - Identification Strategy
Next, we discuss whether draft eligibility induced by random lottery
satisfies IV conditions:
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Relevance
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Vietnam veteran status (joining military service) was not completely
determined by the lottery outcome
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But, draft eligibility (Zi ) and joining military service (Di ) is strongly
correlated
Exclusion Restriction
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Draft eligibility is determined by a randomized lottery
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Accordingly, eligibility should be uncorrelated with confounding
factors affecting lifetime earnings
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No reason to expect a direct effect of eligibility on earnings
IV - Potential Outcomes Framework
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Treatment Assignment
(
1 if assigned to treatment group
Zi =
0 if assigned to control group
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In the study example,
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Zi = 1: those who are eligible for draft (lottery number below cutoff)
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Zi = 0: those who are not eligible for draft (lottery number above
cutoff)
IV - Potential Outcomes Framework
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Potential Treatments
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Diz : treatment status given the value of Z
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Di1 : treatment status if assigned to treatment group (draft eligible)
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Di0 : treatment status if assigned to control group (draft ineligible)
Observed Treatment
(
Di =
Di1
Di0
if Zi = 1
if Zi = 0
or
Di = Zi Di1 + (1 − Zi )Di0
IV - Potential Outcomes Framework
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The variation in treatment Di (veteran status) was not entirely
determined by draft eligibility Zi but also from individual choice
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Thus, we can have Di1 = {0, 1}
I
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Those who were draft eligible could join or not join military service
Similarly, we have Di0 = {0, 1}
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Those who were ineligible for the draft could still join military service
IV - Compliers and Non-compliers
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We can define four types of individuals based on whether they follow
the draft eligibility results:
1. Compliers: Di0 = 0 and Di1 = 1
I Eligible for the draft and joins military service
I Ineligible for the draft and does not join military service
2. Always-takers: Di1 = Di0 = 1
I Always joins military service regardless of draft eligibility
3. Never-takers: Di1 = Di0 = 0
I Never joins military service regardless of draft eligibility
4. Defiers: Di0 = 1 and Di1 = 0
I Eligible but does not join military service
I Ineligible but joins military service
Identification Results for IV
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The IV method characterizes a causal chain from the instrument Zi
(draft eligibility) to outcome Yi (earnings) through the treatment Di
(military service)
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Intuitively, we can write this as
Effect of Instrument (Z ) on Outcome (Y )
= Effect of Instrument (Z ) on Treatment (D)
× Effect of Treatment (D) on Outcome (Y )
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Rearranging this equation, we obtain
Effect of Treatment (D) on Outcome (Y )
Effect of Instrument (Z ) on Outcome (Y )
=
Effect of Instrument (Z ) on Treatment (D)
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Formally, IV can be represented as
αIV =
E [Yi |Zi = 1] − E [Yi |Zi = 0]
E [Di |Zi = 1] − E [Di |Zi = 0]
Identification Assumptions for IV
Assumption 1
Relevance
E [Di |Zi = 1] − E [Di |Zi = 0] 6= 0
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We need the instrument to be significantly related to the treatment
Assumption 2
Independence
(Yi1 , Yi0 , Di1 , Di0 ) ⊥
⊥ Zi
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The IV is independent of potential outcomes and potential treatment
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This assumption is sufficient for a causal interpretation of the
reduced form:
E [Yi |Zi = 1] − E [Yi |Zi = 0]
= E [Yi (Di1 )|Zi = 1] − E [Yi (Di0 )|Zi = 0]
= E [Yi (Di1 )] − E [Yi (Di0 )]
Identification Assumptions for IV
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Independence also means that the first stage captures the causal
effect of Zi on Di :
E [Di |Zi = 1] − E [Di |Zi = 0]
= E [Di1 |Zi = 1] − E [Di0 |Zi = 0]
= E [Di1 − Di0 ]
Assumption 3
Exclusion Restriction
Yid (Z = 1) = Yid (Z = 0) = Yid
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The potential outcomes for each treatment status only depend on
the treatment Di , not the instrument Zi
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Vietnam draft lottery example:
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An individual’s potential earnings as a veteran or non-veteran are
assumed to be unchanged by the draft eligibility status
Violation of Exclusion Restriction
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The exclusion restriction would be violated if low lottery numbers
may have affected the decision to enroll to college (e.g. to avoid the
draft)
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If this was the case the lottery number would be correlated with
earnings because:
1. it affected the likelihood of joining military service
2. it affected the likelihood of educational attainment
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The fact that the lottery number is randomly assigned (which
satisfies the independence assumption) does NOT ensure that the
exclusion restriction is satisfied
Identification Assumptions for IV
Assumption 4
Monotonicity
Di1 ≥ Di0
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Finally, we need to make one last assumption about the relationship
between the instrument and treatment
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This assumption says that the treatment is monotonically increasing
in the instrument
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This is sometimes called no defiers
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In the draft lottery example:
I
there is no individual who would join military service if they were
draft ineligible but would not join if they were draft eligible
Identification Result - IV
Assumption 5
IV Identifies Local Average Treatment Effect (LATE)
αIV =
E [Yi |Zi = 1] − E [Yi |Zi = 0]
= E [Yi1 − Yi0 |Di1 > Di0 ]
E [Di |Zi = 1] − E [Di |Zi = 0]
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IV identifies the causal effect of treatment for compliers (those who
take up the treatment induced by the instrument)
I
In the Vietnam Lottery example, the lottery IV can identify the
causal effect of military service on lifetime earnings for those who
join military service if eligible and not join if ineligible
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Note that IV cannot say anything about the causal effect for always
takers or never takers: Di1 − Di0 = 0
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Defiers are ruled out through the monotonicity assumption
Proof: IV identification of LATE
αIV
=
=
E [Yi |Zi = 1] − E [Yi |Zi = 0]
E [Di |Zi = 1] − E [Di |Zi = 0]
E [Yi1 Di1 + Yi0 (1 − Di1 )|Zi = 1] − E [Yi1 Di0 + Yi0 (1 − Di0 )|Zi = 0]
E [Di1 |Zi = 1] − E [Di0 |Zi = 0]
=
E [Yi1 Di1 + Yi0 (1 − Di1 )] − E [Yi1 Di0 + Yi0 (1 − Di0 )]
E [Di1 ] − E [Di0 ]
=
E [(Yi1 − Yi0 )(Di1 − Di0 )]
E [Di1 ] − E [Di0 ]
Proof: IV identification of LATE (cont’d)
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IV cannot identify causal effect for always takes or never takers:
Di1 − Di0 = 0
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Only for compliers Di1 − Di0 = 1 and defiers Di1 − Di0 = −1
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Monotonicity assumption rules out defiers
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Then, with only compliers we obtain the following:
=
E [(Yi1 − Yi0 )(Di1 − Di0 )]
E [Di1 ] − E [Di0 ]
=
E [(Yi1 − Yi0 ) × (Di1 − Di0 = 1)|Di1 − Di0 = 1]P(Di1 − Di0 = 1)
E [Di1 ] − E [Di0 ]
=
E [(Yi1 − Yi0 ) × (Di1 − Di0 = 1)|Di1 − Di0 = 1]P(Di1 − Di0 = 1)
P(Di1 − Di0 = 1)
=
E [Yi1 − Yi0 |Di1 > Di0 ] = αLATE
IV identifies ATE for compliers
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Never takers and always takers do not change their treatment status
regardless of the instrument status
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Only compliers and defiers contribute to the IV estimate
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The monotonicity assumption rules out the effect from defiers
(should carefully think whether this assumption holds in the research
setting)
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Accordingly, IV identifies the average treatment effect for compliers
Local Average Treatment Effect
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LATE is the average treatment effect for individuals who joined
military service because of the lottery draft outcome
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ATE among the compliers 6= ATE for whole population
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To extrapolate the IV results to never-takers or always-takers we
need to make further assumptions (e.g. homogeneous causal effects)
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Importantly, LATE is different when using different instruments
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Whether or not what the IV identifies (LATE) is interesting depends
on the instrument
LATE and ATT
Special Cases in which αLATE = αATT
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If treatment Di is randomized (e.g. RCT) and Zi = Di then
everybody is a complier
I
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That is, no never-taker or always-taker
With one-sided noncompliance (i.e. no always-taker),
Di1 = {0, 1}, Di0 = 0:
E [Yi1 − Yi0 |Di1 > Di0 ]
= E [Yi1 − Yi0 |Di1 = 1]
= E [Yi1 − Yi0 |Zi = 1, Di1 = 1]
= E [Yi1 − Yi0 |Di = 1]
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Thus,
αLATE = αATT
IV Estimation
We can estimate αIV by running the following two regressions:
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Reduced form regression: the effect of lottery draft on earnings
Yi
αRF
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First stage regression: the effect of lottery draft on joining military
service
Di
αFS
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= µ + αRF Zi + i
Cov(Yi , Zi )
=
V(Zi )
= θ + αFS Zi + νi
Cov(Di , Zi )
=
V(Zi )
The IV estimator is:
α̂IV =
d i , Zi )
Cov(Y
α̂RF
=
d i , Zi )
α̂FS
Cov(D
Two Stage Least Squares (TSLS)
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In practice we often estimate IV using Two Stage Least Squares
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If identification assumptions only hold after conditioning on X ,
covariates are often introduced using TSLS regression
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It is called TSLS because you could estimate it as follows:
1. Obtain the first stage fitted values:
D̂i = θ̂ + α̂FS Zi + X 0 β̂
2. Plug the first stage fitted values into the “second-stage equation”
Yi = X 0 γ + αTSLS D̂i + ui∗
Two Stage Least Squares (TSLS)
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However, this TSLS estimation will give you the wrong standard
errors
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Following the two steps procedure, we calculate the standard errors
based on ui∗
ui∗ = Yi − X 0 γ − αTSLS D̂i
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But what we really want is the standard errors based on ui
ui = Yi − X 0 γ − αTSLS Di
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In practice,
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Stata and other regression softwares will return the corrected
standard errors
Angrist (1990) - Main Results
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First stage results:
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Having a low lottery number (being eligible for the draft) increases
veteran status by about 16 percentage points
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The mean of veteran status is about 27 percent
Second stage results:
I
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Serving in the army lowers earnings by $2,050 - $2,741 per year
Placebo test on exclusion restriction:
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Earnings of 1969 cohort should not be affected by 1970 draft lottery
outcome (draft lottery should affect earnings only through military
service but 1969 cohort was not subject to draft lottery)
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Author finds no evidence of an association between draft eligibility
and earnings among 1969 cohort
Empirical Paper: Angrist and Krueger (QJE, 1991)
Joshua Angrist and Alan Krueger (1991). Does Compulsory School
Attendance Affect Schooling and Earnings? Quarterly Journal of
Economics. 106(4): 979-1014.
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The paper studies the impact of Compulsory Attendance Law (CAL)
on earnings in U.S.
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Influential study in the education literature
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Uses quarter of birth as an instrument for schooling
I
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Some students who are born earlier in the year can legally drop out
whereas students born later in the year have to remain in school until
end of grade
Find that educational attainment and earnings higher for those
compelled to stay longer in school because of CAL
AK(1991) - Institutional Setting
Quarter of Birth and Years of Schooling
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Suppose that the probability of dropout is constant across birthdays
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Schools admit students to first grade only if they reach age six by
January 1 of the academic year they enter
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Students born earlier in the year are older (i.e. reach birthday faster)
than students born later
I
Compulsory Attendance Law requires students to stay in school until
they reach certain age (e.g. 16)
I
Students born in earlier months can legally drop out with less
schooling than students born later
Years of Education and Quarter of Birth in Census Data
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Increasing trend in average education for men born between 1930
and 1950
I
Average education higher for individuals born near end of year than
individuals born early in the year
De-trended Years of Education
where
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Eicj : educational outcome of individual i born in year c and quarter j
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MAcj = (E−2 + E−1 + E+1 + E+2 )/4
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Qicj : dummy for quarter of year birth
Detrended Years of Education and Quarter of Birth
Black bars indicate that
average education of men
born in first quarter less
than men born in surrounding quarters
Earnings and Quarter of Birth
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Men born in first quarter of the year tend to have lower earnings
than men born in nearby months
Baseline Estimates - Returns to Education
Wald =
∆Earnings
∆Education
AK(1991) - Two Stage Least Squares
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The first stage regression is:
Ei = X 0 π10 + π11 Q1i + π12 Q2i + π13 Q3i + Yi θ + i
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The second stage regression is:
Wi = X 0 π20 + π21 Ei + Yi θ + ηi
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Ei : years of education of individual i
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Wi : weekly wage of individual i
I
Yi : year indicator
I
Qi : quarter of birth indicator
What is the reduced form regression?
First Stage Estimation Results
Earlier birth
associated with
less education
⇓
Caused by
(1) CAL or
(2) Other factors
TSLS Estimates - Returns to Education for 1920-1929 Cohort
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Additional year of education increases weekly earnings by 7 percent
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OLS and TSLS provide similar estimates
TSLS Estimates - Returns to Education for 1930-1939 Cohort
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Additional year of education increases weekly earnings by 8 percent
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OLS and TSLS estimates are again quite similar
TSLS Estimates - Returns to Education for Black Men
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Returns to education lower for black men relative to white men: 5%
vs 8%
I
Possible explanation for less returns to education?
Weak Instruments
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As you will know IV is consistent but not unbiased
I
For a long time researchers estimating IV models never cared much
about the small sample bias
I
In the early 1990s a number of papers, however, highlighted that IV
can be severely biased in particular if instruments are weak (i.e. the
first stage relationship is weak) and if you use many instruments to
instrument for one endogenous variable (i.e. there are many
overidentifying restrictions)
I
In the worst case, if the instruments are weak such that there is no
first stage then the 2SLS sampling distribution is centered on the
probability limit of OLS
Weak Instruments - Bias Towards OLS
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Let’s consider a model with a single endogenous regressor and a
simple constant treatment effect
I
The causal model of interest is:
Y = βX + I
(1)
The instrumental variable is Z with the first stage equation:
X = γZ + η
(2)
I
If and η are correlated, estimating equation (1) by OLS would lead
to biased results
I
The OLS bias is:
E [βOLS − β] =
Cov (, η)
Cov (, X )
=
Var (X )
Var (X )
Weak Instruments - Bias Towards OLS
I
It can be shown that the bias of 2SLS is approximately:
E [β̂2SLS − β] ≈
Cov (, η) 1
Var (η) F + 1
where F is the population analogue of the F-statistic for the joint
significance of the instruments in the first stage regression (See
MHE pp. 206-208 for derivation)
I
If the first stage is weak (i.e. F =⇒ 0) the bias of 2SLS approaches
Cov (,η)
Var (η)
I
This is the same as the OLS bias for γ = 0 in equation (2) (i.e.
there is no first stage relationship) implies Var (X ) = Var (η) and
(,η)
Cov (,η)
therefore the OLS bias Cov
Var (X ) becomes Var (η)
I
If the first stage is very strong (F =⇒ ∞) the IV bias goes to 0
Weak Instruments - Adding More Instruments
I
Adding more weak instruments will increase the bias of 2SLS. By
adding further instruments without predictive power the first stage
F-statistic goes towards 0 and the bias increases
I
If the model is just identified, weak instrument bias is less of a
problem
I
Bound, Jaeger, and Baker (1995) highlighted this problem for the
Angrist and Krueger (1991) study which uses different sets of
instruments:
I
quarter of birth dummies - 3 instruments
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quarter of birth + quarter of birth × year of birth dummies - 30
instruments
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quarter of birth + quarter of birth × year of birth + quarter of birth
× state of birth - 180 instruments
BJB (1995) - Adding Weak Instruments in AK (1991)
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Adding more weak instruments reduced the first stage F-statistic
and moves the IV coefficient towards the OLS coefficient
BJB (1995) - Adding Weak Instruments in AK (1991)
I
Adding more weak instruments reduced the first stage F-statistic
and moves the IV coefficient towards the OLS coefficient
What can you do if you have weak instruments?
With weak instruments you have the following options:
1. Use a just identified model with your strongest IV. If the instrument
is very weak, however, your standard errors will probably be very
large
2. Use a limited information maximum likelihood estimator (LIML)
I
This provides the same asymptotic distribution as 2SLS (under
constant effects) but provides a finite-sample bias reduction
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LIML can be estimated in Stata using the ivregress command
3. Find stronger instruments
Empirical Paper: Angrist and Evans (1998)
Joshua Angrist and William Evans (1998) “Children and Their Parents’
Labor Supply: Evidence from Exogenous Variation in Famliy Size”,
American Economic Review. 88(3): 450-477.
I
Paper examines the effect of childbearing on female labor supply
I
The relationship between fertility and labor supply has long been an
interest to labor economists
I
Challenge is selection bias: mothers with low potential earnings
may be more likely to decide to have children
AE (1998) - Identification Strategy
I
The authors solve the selection bias problem using instrumental
variables:
1. Multiple births (twin):
I The occurence of a multiple birth is essentially random and unrelated
to potential outcomes or demographic characteristics
2. Sibling sex composition:
I American parents with two children are much more likely to have a
third child if the first two are of same-sex than mixed-sex
I Possible if American parents prefer having mixed-sex composition
I The same-sex instrument is based on the claim that sibling sex
composition is random and affects mother’s labor supply exclusively
through increasing fertility
AE (1998) - Identification Strategy
I
They want to estimate the effect of childbearing (Di ) on female
labor supply (Yi )
I
Di : having a third birth
I
Yi : employment, weeks worked
I
Two instrumental variables:
1. Twins instrument (Z1i ) is an indicator for multiple births at second
pregnancy in a sample of mothers with at least two children
2. Sibling sex instrument (Z2i ) is an indicator for the first two children
having the same sex
I
If they are both valid IVs would they show similar results?
AE (1998) - Wald Estimates
AE (1998) - TSLS Estimates
AE (1998) - Results
I
Twins and Mixed-sex instruments both suggest that the birth of a
third child has a large negative impact on mother’s employment
status (weeks worked and hours worked)
I
Interestingly, estimate using same sex shows larger magnitude of
effect of childbearing than estimate using twins
I
Different instruments need not generate similar estimates of causal
effect even when both are valid IVs
I
This is because IV only identifies local average treatment effects ATE for compliers
I
Thus, different instruments have different compliers leading to
different LATE
IV in Randomized Experiment with Partial Compliance
I
The use of IV methods can also be useful when evaluating a
randomized control trial (RCT)
I
In many RCTs, actually receiving treatment is voluntary among
those randomly assigned to treatment
I
This is called randomized experiment with partial (imperfect)
compliance
I
I
Those who are assigned to treatment might NOT take up treatment
I
Those who are NOT assigned to treatment might take up treatment
Selection bias: only those who are particularly likely to benefit from
treatment will actually take up treatment
IV in Randomized Experiment with Partial Compliance
I
If we just compare means between treated and untreated individuals
OLS estimates will be biased
I
Since some individuals in the treatment (control) group self-select
into treatment
I
Solution: using randomly assigned treatment Zi as an instrument
for receiving treatment Di
I
This would allow us to estimate the Local Average Treatment Effect
(LATE) - average treatment effect for compliers
Empirical Paper: Bloom et. al. (1997)
Bloom et. al. (1997) ”The Benefits and Costs of JTPA Title II-A
Programs: Key Findings from the National Job Training Partnership Act
Study”, Journal of Human Resources. 32(3): 549-576
I
The paper estimates the effect of the job training program on
earnings
I
The program provides job training to people facing barriers for
employment (e.g. dislocated workers, disadvantaged youth)
Bloom et. al. (1997) - Partial Compliance
I
Among 20,601 sample members, two thirds were assigned to
treatment group, offer enrollment into job training program (Title
II-A), and one third was assigned to control group
I
Only 60 percent of those who were offered the training actually
received it
I
2 percent of people in the control group also received training
I
Authors evaluate the differences in earnings in the 30-month
follow-up period after random assignment
Bloom et. al. (1997) - Partial Compliance
I
Simply comparing those who participate in the job training program
vs. those do not participate will lead to selection bias
I
The authors use random assignment of job training Zi as an IV for
actual job training Di
I
Since compliance problem is largely confined to the treatment group
we have little concern about always taker such that
αLATE ≈ αATT
Bloom et. al. (1997) - Comparison of Estimation Results
Comparisons by
Training Status
Men
Women
Individual
Covariates?
Comparisons by
Assignment Status
I.V.
Estimates
(1)
(2)
(3)
(4)
(5)
(6)
3970
(555)
2133
(345)
3754
(536)
2215
(334)
1117
(569)
1243
(359)
970
(546)
1139
(341)
1825
(928)
1942
(560)
1593
(895)
1780
(532)
No
Yes
No
Yes
No
Yes
I
Columns (1) and (2) show OLS estimates
I
The difference in earnings between those who are trained and those
who are not
I
These estimates could be upward-biased because individuals assigned
to treatment could decline take up of treatment
Bloom et. al. (1997) - Comparison of Estimation Results
Comparisons by
Training Status
Men
Women
Individual
Covariates?
Comparisons by
Assignment Status
I.V.
Estimates
(1)
(2)
(3)
(4)
(5)
(6)
3970
(555)
2133
(345)
3754
(536)
2215
(334)
1117
(569)
1243
(359)
970
(546)
1139
(341)
1825
(928)
1942
(560)
1593
(895)
1780
(532)
No
Yes
No
Yes
No
Yes
I
Columns (3) and (4) compare individuals according to whether or
not they were assigned to treatment
I
This estimate is called intention to treat (ITT) or reduced form
estimate
Intention to Treat (ITT) Effect
I
Since Zi is randomly assigned, the ITT effect has a causal
interpretation
I
It provides us the causal effect of offering treatment (not actually
receiving treatment)
I
In the event of no take-up, the ITT estimate will be smaller than the
average treatment effect on treated
I
To derive the LATE, you divide the ITT by the difference in
treatment rates between the original treatment and control group
αIV =
I
E [Yi |Zi = 1] − E [Yi |Zi = 0]
E [Di |Zi = 1] − E [Di |Zi = 0]
if treatment among control group is negligible (i.e. E [Di |Zi = 0] = 0)
then the denominator is simply the take up rate (i.e. E [Di |Zi = 1])
Bloom et. al. (1997) - Comparison of Estimation Results
Comparisons by
Training Status
Men
Women
Individual
Covariates?
Comparisons by
Assignment Status
I.V.
Estimates
(1)
(2)
(3)
(4)
(5)
(6)
3970
(555)
2133
(345)
3754
(536)
2215
(334)
1117
(569)
1243
(359)
970
(546)
1139
(341)
1825
(928)
1942
(560)
1593
(895)
1780
(532)
No
Yes
No
Yes
No
Yes
I
Columns (5) and (6) show IV estimates - Local Average Treatment
Effect (LATE)
I
Here we actually estimate the ATT (not only LATE) because there
are almost no always takers
I
The treated population consists (almost) entirely of compliers
Practical Tips for IV Strategy
1. Check relevance between instrument and treatment variables
I
Does this IV make sense?
I
Do the first stage coefficients have the right magnitude and sign?
I
Report the F-statistic from the first stage regression
I Stock, Wright, and Yogo (2010) suggest that F > 10 indicate that
you do not have a weak instrument problem
I
If instruments are weak, then the TSLS estimator is biased and the
t-statistic has a non-normal distribution
Practical Tips for IV Strategy
2. Check exclusion restriction
I
The exclusion restriction cannot be tested directly, but it can be
falsified
I
Placebo test
I Test the reduced form effect of Zi on Yi in situations where it is
impossible or extremely unlikely that Zi could affect Di
I Because Zi cannot affect Di then the exclusion restriction implies
that this placebo test should have no effect
3. If you have many IVs pick your best instrument and use the just
identified model (e.g. use one IV with one endogeneous regressor;
two IVs with two endogenous regressors, etc...)
4. The reduced form result as a litmus test
I
If you can’t find a significant relationship in the reduced form
regression then it is probably not there
Next Lecture
Topic 5. Instrumental Variable II
I
I
Empirical papers:
I
Acemoglu, Johnson, and Robinson (2001) “The Colonial Origins of
Comparative Development: An Empirical Investigation”, American
Economic Review. 91(5): 1369-1401.
I
Park, S. (2019) “Socializing at Work: Evidence from a Field
Experiment with Manufacturing Workers” American Economic
Journal: Applied Economics. 11(3): 424-455.
Data session with IV