DDFr@best.com (David Friedman) writes:
> In article <6nptur$dri$1@nnrp1.dejanews.com>, tlambert@my-dejanews.com wrote:
>
> >Here is what Weil actually said:
>
> ...
>
> >] ...Most important, when Lott's
> >] research was published, a number of academic researchers looked at
> >] this methods and his conclusions and determined his research was
> >] fundamentally flawed. The criticism was so convincing that even Gary
> >] Kleck, a criminologist whose work is often cited by John Lott and the
> >] NRA, has dismissed Lott's conclusions. Kleck wrote in his book,
> >] Targeting Guns, that "more likely the declines in crime coinciding
> >] with relaxation of carry laws were largely attributable to other
> >] factors not controlled for in the Lott Mustard analysis."
> >
> >Weil has correctly quoted Kleck, and correctly summarized Kleck's
> >position.
>
> I don't think so. Kleck is asserting, not that Lott's research was
> "fundamentally flawed," but that he suspects the conclusion is wrong,
> which is a very different proposition.
Weil did not say that Kleck asserted that Lott's research was
fundamentally flawed, but that Kleck disagreed with Lott's
conclusions.
> Incidentally, the "number of academic researchers determined ..." part is
> hardly an accurate description of the the scholarly debate. You might want
> to look at my summary of the Black and Nagin paper, which is, I think, the
> only scholarly criticism to have so far been published--it is linked to my
> web site. Most of their piece consists of demonstrating that the
> assumptions of one of Lott's simpler specifications--one in which a shall
> issue law has a state independent and time independent effect--are not
> true, which is hardly surprising; one whould not expect the assumptions of
> a simple specification to be literally true. Black and Nagin mostly ignore
> the fact that Lott went on to run regressions with much more complicated
> specifications, including effects varying by state and over time, and
> continued to get the same pattern.
>
> Suppose you published a regression testing the conjecture that height was
> affected by nutrition. Your specification took the form:
>
> Equation 1: Height=A+Bx(some measure of nutritional adequacy)+random error.
>
> You find that B is positive and significant.
>
> Someone critiques your work as follows:
>
> "The Lambert specification assumes that height does not depend on parental
> height. We may rewrite Equation 1 as:
>
> Height=A+Bx(some measure of nutritional adequacy)+CiPi+random error.
>
> Here Pi is a dummy for the average height of the parents (P1 is 1 if their
> average is below 5'6", 0 otherwise, P2 is 1 if ... ), Ci the coefficient
> on the dummy. Lambert's specification amounts to assuming that all of the
> Ci's are equal. We have done a statistical test of that assumption, and
> demonstrated that it can be rejected at the .01 confidence level. Hence
> his work is fundamentally unsound."
>
> That is precisely what Black and Nagin spend a large part of their paper
> doing.
No it isn't. I think you need to take another look at their paper.
It's more like this "We may rewrite Equation 1 as:
Height=A+Bix(some measure of nutritional adequacy)+random error.
where Bi allows nutrition to have a different effect on different age
groups. Half of the Bi's are positive and half are negative. It is
not reasonable to suppose that nutrition makes 5 year olds taller and 6
year olds shorter."
> >You have been mislead by Lott again. The regression was
> >weighted by population and restricting it to large population counties
> >only removes 31% of the population. Furthermore, if the reduction was
> >caused by conceled carry, this should *strengthen* the result since in
> >the low population counties it was quite easy to get a permit even
> >before the shall-issue laws. Black and Nagin found that when you
> >looked at each state there was no consistent effect on crime, except
> >for assault.
>
> 1. Black and Nagin replicated Lott's Table 3 regression, but omitted the
> overall figure for violent crime--presumably because it is significant.
What a strange thing to presume! They included figures that were
significant, so it is clear that that was not the criterion used for
inclusion.
> 2. In at least one (I think more) of the states, the population
> restriction meant that there was only one county in the sample, so
> anomalous results are hardly surprising. Your point about population is
> correct, but somewhat misleading. Ten small counties will have the same
> weight in the regression as one large county with the same total
> population. But one large county will have one county government, county
> police agency, etc., so there is less opportunity for the effect of
> uncontrolled variables to average out.
>
> Suppose we did the regression twice, once over 2 large counties for ten
> years, once over 100 small ones for ten years. Putting aside the
> particular arguments about differences in county policies, wouldn't you
> find a result in the latter case much more convincing?
Only if there were no other differences, which is clearly not true. I
am puzzled as to why Lott is complaining about restricting the sample
to large counties. In his paper he wrote "the more the sample was
limited to larger population counties the stronger and more
statistically significant was the relationship between concealed
hangun laws and the previously reported effects on crime."
> 3. If you get your sample size low enough, you can always get results to
> be insignificant--and the sample size for a single state is a lot smaller
> than for all states combined. Simply eliminating the low population states
> left the pattern unchanged, except for a drop in significance presumably
> due to the smaller sample. In order to seriously disturb the pattern Lott
> found, they had to first restrict the sample to large counties, then pick
> a state (Florida) to eliminate, then observe that there wasn't much
> pattern left in the data after doing all of that.
No. Even with the full sample, eliminating Florida removes the effect
on murder and rape. Bartley and Cohen got a similar result by looking
at lots of different possible models - the effects on murder and rape
were sometimes positive and sometimes negative. (Though the effects
on assault were consistently negative.)
> Read my webbed commentary, the original article, and Lott's response, and
> then see if you think Black and Nagin have a leg to stand on.
I've read them all and find that I must disagree with you.
> You might
> pay particular attention to my (and Lott's) point about what happens when
> you put in a quadratic time dependent term, state specific--that's the
> point that looks to me most like deliberate dishonesty rather than merely
> an honest attempt to make Lott's work look as bad as possible.
That's the only one where I think you have a point. I also think that
allegations of dishonesty will only generate heat and not any light.
> Incidentally, I believe there is at least one article now published
> independently verifying Lott's conclusion--John can probably provide the
> cite.
Bartley and Cohen, Economic Inqiry 36 p258 April 1998. I read
it. I don't feel that your description of the article is entirely
accurate. They don't think that the Lott-Mustard paper can be
dismissed outright, but also do not think that it is sufficient to
draw strong policy implications.
Tim