In the previous lecture, we saw that not all students that was randomized into the different

treatment arms in project STAR stayed in the groups to which they were allocated.

Some students left the different groups for various unknown reasons.

However as long as reallocation happens randomly it does not invalidate the randomized controlled

trial in terms of estimating the causal effect of the treatment.

However, it is very likely that reallocation of individuals after randomization is not

random. Students allocated to the control group may

be unhappy by not receiving the treatment and might subsequently try to get into treatment

group anyway. In the case of small classes, most students

allocated to small classes are probably happy by being assigned to a small class and will

not try to reallocate but in many other cases some of those allocated to treatment may subsequently

try to defer treatment if possible. For instance training or education for unemployed.

Here it is often the case that many unemployed allocated to training or education does in

fact not want to do this and tries to evade treatment.

All this invalidates randomization and threatens the possibility to estimate the causal effect

of a treatment from a randomized trial. Therefore, even if RCT’s in theory enables

researchers to estimate causal effects, in practice this may prove difficult.

However, surprisingly, even in the case of non-random dropout, data from an RCT still

enables the estimation of causal effects. The following slides explains how.

Denote as before T the treatment indicator, taking the value one if the individual is

actually treated that is not only allocated to treatment but also actually treated and

zero if not treated. Further, define Z equal to one if allocated

to the treatment group and zero otherwise. Z is the randomization indicator.

Again the observed outcome is outcome either as treated or untreated.

Average outcome for those offered treatment is the average outcome without treatment for

those offered treatment plus the treatment effect (the difference between outcome with

and without treatment) for those actually treated (obtained by multiplying with the

treatment indicator) for those allocated to treatment.

Because allocation into treatment is randomized, the average baseline outcome for those allocated

into treatment is equal to the baseline outcome for those not allocated into treatment.

Now write the average gain if treated for those allocated to treatment (Z=1) separately

for those who choose not to receive treatment (T=0) and those who choose to receive treatment

(T=1). A fraction of those offered treatment declines

and one minus this fraction accepts. The gain for those who decline treatment is

zero, as they are not treated. The gain for those who accept treatment can

be rewritten as the gain conditional on being offered treatment (z=1) and accepting treatment

(T=1). We can now rewrite the average gain for those

treated (both those accepting treatment and those declining) as a weighted average of

the gain for those accepting and those declining treatment.

Further, we assume that no one can enter treatment without being offered treatment – that is

we exclude the possibility that you can sneak into treatment without being offered treatment.

Thus we only allow for dropping treatment if offered.

Hence, if you accept treatment it must have been offered, that is if T = 1, this implies

that z = 1 (but not necessarily the other way around).

From this, it also follows that the average gain for those offered and accepting treatment

is the same as the average gain for those who accepted treatment – so we do only need

to condition on that people accept treatment. From this, we are now able to derive the main

results – the “Bloom” equation named after its inventor, Howard Bloom.

On the left hand side of the equation, we have observed entities, that is, stuff that

we can calculate from the observed data and on the right we have our object of interest,

the average treatment effect for those treated. This implies that we can calculate the average

treatment effect for those who accepted treatment even if some individuals selectively leaves

treatment. Now given the algebra on the previous slide,

we can now prove the “Bloom” equation. First, the average outcome for those offered

treatment can be rewritten as the average baseline for those offered treatment plus

the average gain for those who accept treatment conditional on being offered treatment.

That is equal to the baseline outcome for those not offered treatment (due to the RCT)

plus the gain for those offered and actually treated.

This is, again, equal to the average baseline for those not offered treatment plus the weighted

average gain for those offered and accepting and those declining treatment.

This is equal to the average baseline outcome for those not offered treatment plus the average

gain for those offered and accepting treatment weighted with the fraction who accept treatment

when offered treatment. Going back to the Bloom equation at the top

of the slide, we can write the average outcome for those not offered treatment as the baseline

outcome for those not offered treatment – as this group is not treated and they are thus

unaffected by the treatment but otherwise equal to those offered treatment.

Collecting everything, we can write the nominator of the left hand side of the Bloom equation

as the baseline outcome for those not offered treatment plus the weighted gain for those

offered and accepting treatment minus the average outcome for those not offered treatment.

As can be seen everything but the right hand side of the Bloom equation nicely cancels

out leaving the right hand side of the Bloom equation.

This concludes the proof. So you have just seen that despite non-random

dropout from an RCT, we can still estimate the causal effect of the treatment for those

who accept treatment. Note that this is NOT the same as the average

causal effect for those offered treatment (including those who rejects treatment and

this has zero effect). We will never know what would have happened

to those who declined treatment, as this is not necessarily the same as what happened

to those accepted treatment due to selective drop out.

We now turn to something different. When persons are selected into treatment,

they are obviously aware that they are exposed to the treatment.

This, by itself may affect behavior. Therefore, while we can measure the causal

effect of the treatment, the interpretation is less clear if people respond to merely

being observed to a treatment. Do people change behavior because they are

affected by the treatment or because they know they are being observed? This phenomenon

is known as the Hawthorne effect, names so after the famous Hawthorne plant where researchers

try to manipulate productivity by changing the work environment.

However, it was later speculated that worker response was more due to being observed than

to change in work environment. Therefore, change in productivity was not

a result of change in work environment but from being observed by researchers.

Therefore, research did not imply that change in work environment affects productivity but

that being observed affects productivity, at least while being observed.

Later, other researchers has doubted the so-called Hawthorne effect and concluded that the whole

research design was flawed and that the data does not allow either conclusion.

However, to illustrate the idea behind the Hawthorne effect, we look at the STAR data.

The table on the slide shows class size by treatment arm – small classes, regular classes

and regular classes with a teacher’s aide. From the table it can be seen that for classes

of size 16 to 18 students, there are a number of classes of equal size in all three treatment

arms. Thus, if it is the actual class size that

matters and not treatment type, outcomes should be the same in all three treatment arms when

actual class size is the same. If it is a Hawthorne effect, there should

be a difference across treatment arms for the same class size.

Some caution should be considered here, though. Because, even if students are allocated into

treatments by lottery, actual class size could be a result of selective attrition and drop

out after the lottery. If we are willing to assume that ordinary

classes that are observed to be small is a result of negative selection (a bad teacher

for example) and small classes that are in high range for small classes is a result of

positive selection (a good teacher) we should expect that the causal difference between

class types is larger than the observed difference. Thus the estimated difference between treatments

arms for comparable class size is a lower bound for the true difference.

With the above caveat in mind the regressions on this slide shows the difference in math

achievement in kindergarten for students in the different treatments arms.

Students in small classes is the reference group.

The regression results in the top panel shows results for classes in the range less than

29 students and larger than 12 students, and the bottom shows results for classes with

less than 19 students and more than 16 students. This is the range from the table on the previous

slide, where all treatment arms has classes of comparable size.

From the regressions, we find that the effect of treatment arm is the same, irrespective

of whether we look at all class sizes or classes where class size is approximately the same

across treatment arms. Therefore, with the caveat from the previous

slide about the causal effect in the lower panel probably being larger than the estimated

effect, we are inclined to conclude that the causal effect of being in a small class is

more likely to be a Hawthorne effect rather than being an effect of being taught in a

small class. Therefore, when teachers and/or students are

allocated into a small class in the STAR study, this induced them to teach/study harder, not

because they are in a small class but because they are expected to perform better from being

in a small class. You should note that this example is made

up for illustrative purposes of this course and that there is not a general agreement

among researchers that the effect of the STAR project was a Hawthorne effect.

Until now, we have relied upon randomization to infer the causal effect from a treatment.

The upside of this was that it is the design that allowed the researcher to infer causality

and in principle, causality is undeniable. The downside is the external validity.

Is the observed causal effect due to the mechanisms of the treatment or is it a Hawthorne effect?

If a randomized controlled trial is infeasible or if we want to rule out Hawthorne effects,

there are alternative designs; one of the most notable, is called the instrumental variables

method. The basics of instrumental variables will

be laid out on the following slides and then the analogy to the estimator for the randomized

controlled trail will be explained. Say we want to estimate the return to education

by running a regression of log earnings on years of education.

Then we have learned that it would be dangerous to interpret the regression coefficient as

the causal effect of years of education on log earnings unless we have either randomized

years of education or that we have the full set of confounders that affect log earnings

over and above years of education. So, in the absence of data from an RCT on

years of education, what to do? Imagine that we have available a third variable,

z, that affects education but is otherwise uncorrelated with earnings.

Think of z as a variable that when it changes, causes changes in the level of education but

it has no direct effect of earnings. One example could be an educational reform

that expands the minimum years of compulsory school.

It certainly affects years of education but it is very unlikely that it affects individual

earnings over and above education. Obviously other things than a school reform

may affect education. This is indicated by the error term u.

Also, other things than education may affect earnings.

This is indicated by the error term e. It is also very likely that e and u are correlated

as they both capture the effect of stuff, e.g.

intelligence that determines the level of education and earnings.

We may write the figure as equations instead. One equation for the level of earnings, y,

and one equation for the level of education, x.

The instrumental variable only affects the level of education and NOT earnings.

Hence, it should not appear in the equation for earnings.

Note the resemblance to the treatment indicator z previously.

In an RCT, z is the indicator of whether the subject was allocated to the treatment or

control group and T was the indicator of whether treatment was actually accepted.

Here T is replaced by years of education, x.

However, the algebra is the same. Because we can estimate the causal effect

on the treated using randomization into treatment, we can also estimate the causal effect of

years of education because z (e.g. the school reform) acts as a randomizer.

In order for the instrument to deliver causal effects we need it to be independent of everything

else, just a randomization is independent of everything in the case of the RCT.

Therefore, given years of education, x, the school reform, z, must not have any direct

effect on earnings, y. This in turn implies that z must be uncorrelated

with what otherwise affects both years of education as well as earnings.

What follows does not seem to relate to how we derived the Bloom equation.

We return to this in a couple of slides. Instead, we turn to how we derived the linear

regression coefficient, now with the extension of the instrumental variable equation.

We start by working with covariance between the dependent variable and the instrument.

Inserting the expression of the dependent variables in terms of the x variable leads

to that we can rewrite the covariance between y and z as the effect of x on y, b, times

the covariance between x and z plus b times the covariance between e and z.

This implies that we can write the fraction of the covariance between y and z and the

covariance between x and z using the above expression of the covariance between y and

z and this gives us b plus a term involving b and the fraction between the covariance

between e and z and the covariance between x and z.

The denominator, the covariance between e and z is zero by assumption.

Hence, the fraction between the covariance between y and z and the covariance between

x and z is equal to b, the causal effect of x on y.

Therefore, the availability of an instrument allows us to estimate the causal effect of

x on y even when x and the error term, e are correlated.

As an example of instrumental variables in the case of the return to education, we use

the well-known case of quarter of birth; see e.g.

Angrist and Krueger (1995). The idea here is that due to the quarter of

birth, there is variation in when a person can leave compulsory school.

All pupils starts in compulsory school at the same date but might leave when they turn

15. As quarter of birth vary across respondents

but school start does not, quarter of birth might affect the educational level of the

respondents as some pupils are allowed to leave compulsory sooner than others.

This is in fact the case as the top figure shows.

Using US panel data on birth cohorts from the 1930’s we find clear seasonal patterns

in the mean years of education. Thus, quarter of birth, in part, affects your

level of education. This is a graphical illustration of the covariance

between the instrument (z – quarter of birth) and the independent variable (x – years

of education). The next figure shows the covariance between

log earnings and quarter of birth. Here we also find a clear seasonal pattern.

Log earnings partly depends on your quarter of birth.

If the instrumental variable assumption is correct – that the instrumental variable

only affects dependent variables through the independent variables, the reason for quarterly

change in earnings is due to an indirect effect through earnings.

Note that there is no empirical way of verifying the instrumental variable assumption.

It remains an assumption. But if it is true, the ratio between the data

in the two figures yields the causal effect of education on earnings.

We can derive the IV estimator in an alternative way that may be a little more intuitive.

In the first stage, we regress x – years of education, on the instrument – here quarter

of birth. For simplicity think of z as a binary dummy

variable, taking the value one if the respondent is born in the first quarter and zero otherwise.

From this we can obtain the predicted values of x given z.

The virtue of the predicted values of x using z is that the predicted values of x only pertain

the part of the variation in x that is common with z.

Because z is independent from the error term u, by the IV assumption, the predicted value

of x using z is also independent from u. In the second stage, we use the predicted

values of x instead of the observed values of x.

Note that the predicted values of x are also independent of e, again by the IV assumption.

Using the covariance operator we can formally show what was verbally derived on the previous

slide. Essentially, we are estimating the slope of

x on y using predicted rather than observed values of x.

So the IV estimator is the covariance between y and the predicted values of x divided by

the variance of the predicted values of x. Replacing the predicted values of x by their

expression in terms of the instrument z, we get the regression coefficient of z on x multiplied

by the covariance between y and z divided by the variance of z.

Plugging in the definition of the regression coefficient of z on y we finally get that

the IV estimator, the covariance of y and z divided by the covariance of x and z.

Note that this is not at proof that the IV estimator consistently estimates b – it

just shows that we get the IV estimator if we use the two stage estimation procedure

from the previous slide. However, we saw that the IV estimator was

consistent on slide 10. We now conclude the derivations of the IV

estimator by showing the analogy to the Bloom equation.

Imagine that the instrument is binary – as in the example with quarter of birth in either

the first or the last three quarters. It can then be shown that the usual IV estimator,

that is the covariance between y and z divided by the covariance between x and z can be rewritten

as the ratio between the difference between the expected values of y across outcomes of

the instrument and differences between expected values of x across outcomes of the instrument.

This is also known as the Wald estimator. If we replace the dependent variable x with

actual treatment and the instrument as whether individuals are randomized to treatment or

control this is exactly the Bloom equation. So in the IV case, the IV can be thought of

as replacing the lottery in the randomized controlled trial.

Actually, what the IV does, is that it replaces the randomization by design with randomization

by nature. Somehow, “nature” makes the randomization.

To clarify the latter point we show some examples on the next slide.

Imbens and van der Klaauw (1995) studies the effect of being having served in Vietnam on

subsequent earnings. The idea is that having served in Vietnam

may have reduced the earnings capacity of veterans due to lost labor market experience

on the “ordinary” labor market or psychic disorders, such as posttraumatic stress disorder

due to combat experience. However, one could imagine that those serving

in Vietnam are not comparable to those staying at home.

Even though drafting to serve in the army was made by lottery, exemptions was possible,

the former US president Bush being a notable example.

Therefore, Imbens and van der Klaauw use cohort indicators as instrumental variables.

If one is willing to assume that, there are no differences in earnings capacity across

cohorts, being born in a different cohort’s yields “lottery” like differences in drafting

probabilities independent of earnings. McClellan et al.

(1994) study the effect of heart attack surgery on health.

However, people hospitalized for heart surgery may not be randomly selected.

People with health insurance or people with knowledge of health problems may be more likely

to be hospitalized than others. To generate lottery like variation in hospitalization

McClellan et al. uses proximity to cardiac health care facilities.

For individuals with the same background characteristics but different proximity have different opportunities

for getting into surgery in time. Evans and Ringel (1999) studies the effect

of maternal smoking on fetal birth weight. But it is very likely that women who smoke

during pregnancy have a different health profile than women who do not smoke during pregnancy.

Therefore, it would not be safe to assume that the entire average difference in birth

weight across women who smoke and do not smoke are the causal effect of smoking.

To generate lottery like variation in smoking Evans and Ringel uses state cigarette taxes.

As taxes vary across states, this is thought to generate differences in smoking habits

across otherwise identical women. In this lecture, you have learned that even

though there may be selective dropouts from RCT’s one may still be able to estimate

the causal effect of a treatment for those actually treated.

Further, you have learned that it is possible to estimate causal effects in the absence

of data from an RCT. What is needed is something else that generate

lottery like variation in the exposure of the dependent variable.

If such variation is available, one can use the instrumental variable approach to estimate

causal effects. In the next and final lecture, you will learn

even less restrictive methods that also may be able to yield causal estimates form non-randomized

data.

Lecture 4 - Instrumental Variables

Measuring Causal Effects in the Social Sciences

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