Sample problem set which received max. grade
Applied Microeconometrics I
Problem Set 5
1. How Responsive is the Investment in Schooling to Changes in Redistribution
Policies and in Returns? (Abramitzky and Lavy 2014)
1) They are trying to assess how an increase in the rate of return to education, brought
about by a change in redistributive policies, affects students’ choices to invest in
education.
2) They use a differences-in-differences identification strategy for a sample of high
school students living in several Kibbutzim in Israel. Traditionally, Kibbutz people
shared their earnings equally, which implied a practically zero rate of return to
education. Due to mostly external economic conditions, several Kibbutzim switched
from equal sharing to productivity-based wages, implying a sudden large increase in
the rate of return to education. Since the timing of this reform varied across
Kibbutzim, the authors are able to investigate the effect of the increase in the rate of
return to education on educational attainment by conducting a differences-indifferences analysis using students from Kibbutzim that adopted the reform early on
and from those that adopted it later. Specifically, they compare several educational
outcomes of 10th grade students from Kibbutzim that reformed in 1998-2000 (the
treatment group) to those from Kibbutzim that reformed in 2003-2004 (the control
group). They measure the outcomes for cohorts both before the early reforms (10th
graders in 1995 and 1996) and after the early reforms but before the late reforms
(10th graders in 1999 and in 2000), and use these to construct the DID estimates for
different education outcomes. The key identifying assumption is that trends in
education attainment would have evolved similarly in the control group and in the
treatment group, had there not been a reform in the latter.
3) While the internal validity of the study seems to be quite good, there are some
threats to the identification strategy that may question the internal validity. First, the
treatment and the control group may have had different time trends in educational
outcomes over the period of interest. The authors do show that the treatment and
the control group were largely similar in terms of observables both before and after
the treatment, and in terms of educational outcomes before the treatment.
Furthermore, they estimate time trends in educational outcomes for pre-treatment
period, and show that the control and the treatment group evolved similarly during
this period. Neither observation is, however, sufficient for similarity of time trends in
educational outcomes. It could be, for example, that the Kibbutzim that reformed
early had a better understanding of the changing external (economic) conditions,
something which could have increased educational attainment in the treatment
group compared to the control group in the coming years even without the pay
reform. Second, strictly speaking the authors identify the effect of the reform, which
may be different than the effect of an increase in the rate of return to education, for
example because the reform also affects parents’ income, which may have had a
positive effect on education attainment.
4) The study has limited external validity. Clearly, the Kibbutzim are very special cases
of human interaction in the first place. For example, social norms and social
preferences in Kibbutzim are likely quite different to those in market societies.
Ideologically and in terms of sheer magnitude, the reform introduced in them is
nothing short of revolutionary. Hence, reactions to smaller-scale changes in tax rates
and/or in returns to education may be quite different in market economies where
pecuniary and non-pecuniary incentives likely interact in a very different way than
in the Kibbutzim.
2. Does death penalty save lives?
1) My identification strategy is to construct a differences-in-differences estimate
for the effect of death penalty on murder rate. I will utilize the policy change of
1976 when the temporary death penalty moratorium was removed. My control
group consists of states where death penalty was still illegal after the removal,
and my treatment group consists of those states that (re-)introduced death
penalty after the moratorium was removed. Thus, I will observe the average
murder rate in the control group and in the treatment group both before the
removal (1975) and after (1976), and use these to construct the DID estimate.
2) They do. I verify this graphically by plotting the mean murder rates by year for
both the control and the treatment group (see the graph below). There is a
difference in levels but the difference seems to be rather constant across years.
Moreover, in the DID regression, none of the coefficients for TREATMENTxYEAR
interactions seem to be statistically significantly different from zero. This
simply means that the level difference in mean murder rates between the
treatment and the control does not vary across years.
3) The key identifying assumption is that the mean murder rate in the treatment
group would have evolved similarly to that in the control group even in the
absence of the moratorium removal. This guarantees that the control group
serves as an appropriate counterfactual for the treatment group. The
assumption may not hold for various reasons that question the internal validity
of the study. First, there might have been other policy changes in 1976 that may
have affected the groups differently. Second, the control group may have been
affected by the treatment, e.g. through people living in the border of two states
belonging to different groups and incorrectly perceiving the relevant death
penalty policy.
4) The differences-in-differences estimate for the effect of death penalty on
murder rate is 0.106, meaning that, if anything, introducing death penalty
brings about one murder more annually per one million residents. However, the
estimated standard error (clustered) in my case is 0.486, meaning that the
effect is not very precisely estimated. In fact, the estimate is clearly not
statistically significantly different from zero. A 95% confidence interval is
[-0.8453017,1.058289]. Hence we can say pretty confidently that the causal
effect lies somewhere between a reduction of 8.5 murders/million residents
and an increase of 10.5 murders/million residents. That is, we do not learn a lot.
*******Problem Set 5*******
##Question 2
library(multiwayvcov)
##Reading in the data
dp=read.dta("UCR 1960-2003 - problem set 5.dta")
head(dp)
dim(dp)
##State number 22 is Maine
dp[dp$stid==22,]
##Dropping Maine
dp <- dp[dp$stid!=22,]
##Concentrating on the removal of the death penalty moratorium in 1976.
##Hence, I will concentrate on the period 1972-1976.
length(dp[dp$legal==0 & dp$year==1975,"state"])
length(dp[dp$legal==0 & dp$year==1976,"state"])
##There are 22 states in which death penalty was still illegal after the
removal
##of the moratorium in 1976. This is my control group. All other states
##were affected by the removal, and form my treatment group.
##Dropping irrelevant observations.
dp2 <- dp[dp$year>=1972 & dp$year<=1976,]
dim(dp2)
##Creating the treatment dummy
dp2[dp2$state %in% dp2[dp2$legal==1 & dp2$year==1976,"state"] ==
TRUE ,"treatment"] <- c(1)
dp2[dp2$state %in% dp2[dp2$legal==0 & dp2$year==1976,"state"] ==
TRUE ,"treatment"] <- c(0)
##Checking that the treatment variable was correctly assigned.
setequal(dp2[dp2$treatment==0 &
dp2$year==1976,"state"],dp2[dp2$legal==0 & dp2$year==1976,"state"])
##Checking graphically for parallel trends in pre-treatment period.
x <- c(1972:1976)
mean_control <- c(1:5)
mean_treatment <- c(1:5)
for (i in x){
mean_control[i-1971] <- mean(dp2[dp2$year==i &
dp2$treatment==0,"murderrate"])
}
for (i in x){
mean_treatment[i-1971] <- mean(dp2[dp2$year==i &
dp2$treatment==1,"murderrate"])
}
plot(x,c(6:10), type="n", xlab="Year", ylab="Murder rate (annual
murders/100 000 residents)", main="Mean murder rates")
lines(x,mean_control, type="l", col="red")
lines(x,mean_treatment, type="l", col="blue")
legend(1974,7.0, c("Treatment","Control"), lty=c(1,1),
lwd=c(2.5,2.5),col=c("blue","red"))
##Factorizing variables "year" and "state".
dp2$year.f <- factor(dp2$year)
dp2$state.f <- factor(dp2$state)
##Running the DID regression with state dummies as controls.
model <- lm(murderrate ~ treatment + treatment*year.f + state.f, data=dp2)
summary(model)
##Standard errors are incorrect. Using "multiwayvcov" package to get
clustered
##standard errors.
vcov.clust <- cluster.vcov(model, dp2$state)
dim(vcov.clust)
se.clustered.interactions <- c(1:4)
for (i in c(1:4)){
se.clustered.interactions[i] <- sqrt(vcov.clust[54+i,54+i])
}
##Creating 95% confidence intervals for the treatment X year interactions
##using the clustered standard errors.
for (i in c(1:4)){
cat("Treatment X ",1972+i,": [", model$coefficients[55+i]1.96*se.clustered.interactions[i], ", ",
model$coefficients[55+i]+1.96*se.clustered.interactions[i],"]\n")
}
##Calculating the differences-in-differences estimate in two ways.
##Straightforwardly using the group means in 1975 and in 1975 calculated
above.
DID <- (mean_treatment[5]-mean_treatment[4])-(mean_control[5]mean_control[4])
##Utilizing the DID regression "model". The DID estimate is the coefficient
##on treatment:year.f1976 minus the coefficient on treatment:year.f1975.
length(model$coefficients)
model$coefficients[59]-model$coefficients[58]
##The two methods naturally yield the same estimate.
##The estimated variance for the estimator can be calculated as the sum of
the
##estimated variances of the coefficients for treatment X 1976 and for
##treatment X 1975 minus 2 * their estimated covariance.
variance <- vcov.clust[58,58]+vcov.clust[57,57]-2*vcov.clust[57,58]
##Hence the standard error is
sqrt(variance)
##The 95% confidence interval is given by
cat("[",DID-1.96*sqrt(variance),",",DID+1.96*sqrt(variance),"]")