Question: In Table 4.1.1 (p. 124), how are there 30 instruments in Column 8 rather than 27 (= 3 qob dummies * 9 year of birth dummies)?

Why indeed?  There are still 3 QOB main effects.

JA

I had a question regarding LATE. In your book you say in a model with
covariates, 2SLS leads to a sort of "covariate averaged LATE" even
when one does not have a saturated model. Does this mean that as one
introduces covariates the 2SLS estimator is most likely to change and
that change in the 2SLS estimate is not a comment on the validity of
the instrument?However in your empirical examples you seem to suggest
that invariance of 2SLS estimates to introduction of covariates is a
desirable thing.For example in the first paragraph on pg-152 of
Chapter 4, below Table 4.6.1, you state, "The invariance to covariates
seems desirable: since the same-sex instrument is essentially
independent of the covariates, control for covariates is unnecessary
to eliminate bias and should primarily affect precision." Essentially
my question is: should I start worrying if I see my 2SLS estimates
change as I introduce more covariates in my model? Thanks

Wow, awesome question!  MHE is indeed a little fast and loose on this.
Let me take a stab at clarification.

In Section 4.6.2, we talk about how models with covariates can be
understood as generating a weighted average of cov-specific LATEs across
covariate cells.  True enough ... if the the instrument is
discrete and the first stage saturates (includes a full set of covariate
interactions).  So far so good.  Of course, in practice, you might not
want to saturate.  OK, so do Abadie kappa weighting and get the
best-in-class linear approx to the fully saturated model.
Too lazy to do Abadie?  Just do plain old 2SLS, and that will likely be
close enough to a more rigorously justified approx or weighted average.

Later, however, as Nikhil notes - below table 4.6.1 and on the following page -
we express relief (or satisfaction at least) when IV estimates come out
insensitive to covariates (using samesex) on the grounds that samesex is
independent of covs.  

Contradiction? 

Marginal LATE, that is, LATE with no covs, is also a weighted average
of covariate-specific LATE.  The weight here is the histogram of X 
(convince yourself of this using the law of iterated expectations).
Now, sticking the covariates in and saturating (where we start in 4.5.2)
produces a weighted average with different, more complex, weighting scheme
(instead of the histogram of X as for marginal LATE, it's the histogram
times the variance of conditional-on-covs first-stage, as in Thm 4.5.1).
In practice, tho, w/o too much heterogeneity, we don't expect weighting
this way or that to be a big deal.  On the other hand, even under constant
effects, covs may matter big time when there's substantial omitted variables.
bias. Seeing that randomly assigned instrument generates IV estimates
invariant to covs makes me happy - as always, its the OVB I worry about first!  

So to be specific - Nikhil asks if he should worry when IV ests are
sensitive to covs - I'd say, yes, worry a little.
Try to figure out if what you thought was a good instrument is in
fact highly confounded with covariates. If so, its maybe not such a
great experiment after all.   If not, then perhaps the senitivity you're
seeing is just a difference in weighting schemes at work

JA

Question: You state:

“Our view is that regression can be motivated as a particular sort of
weighted matching estimator, and therefore the differences between
regression and matching estimates are unlikely to be of major
empirical importance” (Chapter 3 p. 70)

I take this to mean that in a ‘mostly harmless way’ regular OLS
regression is in fact a method of matching, or is a matching
estimator.  Is that an appropriate interpretation?  In ‘The Stata
Journal and his blog, Andrew Gelman takes issue with my understanding,
he states:
“A casual reader of the book might be left with the unfortunate
impression that matching is a competitor to regression rather than a
tool for making regression more effective.”
Any guidance?

Well Matt, Andrew Gelman’s intentions are undoubtedly good but I’m afraid he risks doing some harm here.  Suppose you’re interested in the effects of treatment, D, and you have a discrete control variable, X, for a selection-on-observables story.  Regress on D an a full set of dummies (i.e., saturated) model for X.  The resulting estimate of  the effect of D is equal to matching on X, and weighting across covariate cells by the variance of treatment conditional on X, as explained in Chapter 3.  While you might not always want to saturate, any other regression model for X gives the best linear approx to this version subject to whatever parameterization you’re using.

This means that i can’t imagine a situation where matching makes sense but regression does not (though some my say that I’m known for my lack of imagination when it comes to econometric methods)

JA

could it be ... MHE

as seen at the University of Groningen . . .what a good-lookin crew!

excellent wardrobe choices

what are they spelling?  I wish I knew

SMYE forever

Question: I have questions about "bad control" (BC) (Section 3.2.3, p.
64). Your prescription is to leave the BC out of the model, or else to
have strong theory for leaving it in. In the stats literature, there
is discussion of "principal stratification" (PS). Let w_0i, w_1i be
the potential outcome of a mediator variable (following the notation
on p. 65) for individual i. The idea of PS is to divide the sample
into, e.g., {i: w_0i = w_1i} and {i: w_0i != w_1i}. These strata are
generally unobservable, but we could otherwise use them as
pre-treatment covariates. Some stats papers argue that the LATE relies
on a special case of PS, where the sample is divided into those whose
treatment status is affected by the instrument, and those whose
treatment status is not. Here, the treatment would be a BC (in the
reduced form, I suppose...?). So why doesn't PS make us more hopeful
about BC? Also, given random treatment, why can't we just instrument
the BC, since it's just another endogenous variable?

Question: My understanding of a difference in difference model is that
the two groups should exist before a policy takes affect (e.g. two
states, companies, school districts).  I was studying the impact of a
policy on an outcome where the two groups did not exist until the
policy went into effect and everyone was eligible for the policy all
at once.  There was no staggered implementation.  Because of this I
thought to use a lagged dependent variable model to study the impact
of the taking advantage of the new program offered through the policy.
 DVt1= Program + DVt-1 + error.  This model would at least allow me to
control for the separate groups in time two.  I recently saw someone
publish on my topic but they used a difference in difference model.
They assigned the program status which in reality could only occur in
t1 after the policy went into affect to the same people in t-1 when
the program did not exist. I did not think this was correct, thus I am
writing for clarification.

thanks for your question Mel

check out the classic training evals by Ashenfelter (1978) and Ashenfelter
and Card (1985).  They compare pre and post for trainees and controls.
They don't know who is a trainee until "period 2." Once training status
is known, however, it's easy to reach back (in a panel) for pre-treatment
obs for both groups.  

Is this a credible identification strategy?
Probably not as good as being able to make an ex ante T and C distinction,
but sometimes ok.
well, when is this ok . . .
Check out the originals and find out!  These classics do a great job of
explaining why and when this sort of DD makes sense . . .

JA