Saturday, May 21, 2011

A Critique of Carpenter and Dobkin (2011)

Recently, a new study by economists Carpenter and Dobkin (2011) has apparently concluded that lowering the drinking age from 21 to 18 will lead to an 8% increase in deaths among 18-20 year olds.  The authors argue that those who are proposing lowering the drinking age would therefore face "a very high burden of proof" for their position.  However, there is less to this study than meets the eye, and we at Twenty-One Debunked do not agree with their conclusions.  In fact, much of what the study adds actually can be said to fuel our side of the debate rather than the pro-21 side, and the burden of proof actually falls on them, not us.

The first part of their study separately examines daytime and nighttime traffic fatality rates (from FARS) from 1975-1993 for four age groups:  15-17, 18-20, 21-24, and 25-29.  (Nighttime deaths should be affected much more than daytime ones since the former are much more likely to involve alcohol.) They use a fixed-effects panel regression that, while it controls for state and year fixed effects, state-specific trends, and population changes, still fails to control for any other variables that would not be subsumed under these (in contrast to Miron and Tetelbaum (2009) and Dee and Evans (2001)).  The drinking age was expressed as the proportion of 18-20 year olds who are legal to drink in a given state-year, hence the expected sign is positive.  The results are summarized below as percent changes, with statistically significant values (p < 0.05) in bold:

Age  Group% Change (Night) % Change (Day)

As one can see, the apparent effect occurred among all age groups rather than just the 18-20 year olds who were targeted by the changes in the legal drinking age.  For 15-17 year olds (the spillover group), whose effects were statistically insignificant, the day-night counterfactual does not appear to work would be predicted if banning 18-20 year olds from drinking really saved the lives of the former.  However, it does appear to work for 21-24 year olds and 25-29 year olds, both of whom should not have been affected by the change in the drinking age since the age groups were evaluated contemporaneously rather than as cohorts.  In fact, the effects on 18-20 year olds and 21-24 year olds are rather comparable, as opposed to a mere spillover which would be much smaller in magnitude.  Thus, it is very likely that the drinking age was a proxy for something else, i.e. one or more of the many possible variables that was not controlled for such as anti-drunk driving campaigns or tougher DUI laws.

We should compare this to other studies that looked at the effects on various age groups.  Miron and Tetelbaum (2009), who thoroughly debunked the idea that the 21 drinking age saves lives (at least in the long run) for 18-20 year olds, found that a legal drinking age higher than 18 has no effect either way on 21-23 year olds but actually increases under-18 driver fatalities.  Dee and Evans (2001) found that a drinking age of 18 or 19 (relative to 21) increases traffic fatalities among 18-19 year olds but decreases fatalities among cohorts of 22-24 year olds who were allowed to drink at 18 or 19, with no consistent effect on 16-17 year olds.  This echoes Asch and Levy (1987 and 1990) and Males (1986), who both found that raising the drinking age to 21 likely just shifts traffic deaths from 18-20 year olds to 21-24 year olds and possibly even increases the net probability of dying by age 25.  In addition, a new, award-winning paper by Dirscherl (2011) finds that raising the drinking age to 21 not only shifts deaths from 18-20 year olds to 21-24 year olds, but actually leads to a net increase in deaths among 18-24 year olds, a phenomenon we like to call "White Noise Syndrome".

Next, the authors examined the effects of the drinking age on the mortality rates of various causes of those same four age groups.  These death rates were gleaned from vital statistics from the National Center for Health Statistics, and the panel estimates of the effects were obtained from a similar model to the one discussed above.  Again, the expected sign is positive.  The results are summarized below, with statistically significant values (p < 0.05) in bold:

Age Group% Change
% Change
% Change
% Change

We see that only for suicide is the effect statistically significant for 18-20 year olds and at the same time insignificant (and smaller) for the other age groups.  That is, only for suicide can one actually infer a potentially significant lifesaving effect of the 21 drinking age.  For traffic fatalities and other external causes of death, there now seems to be a greater effect for 21-24 year olds than for 18-20 year olds, which casts doubt on whether these effects were actually due to the drinking age.  Interestingly, homicide and alcohol-related deaths (e.g. alcohol poisoning, etc.) were not only statisically insignificant in all cases but even had the "wrong" sign for most of the age groups.  Finally, for all-cause mortality, we see that none of the estimates are significant, not even at the 10% level, which means that they are likely due to chance (and thus spurious).  However, the above results are nonetheless taken by the authors of the study to indicate an overall lifesaving effect.

In a previous post, we at Twenty-One Debunked ran several difference-in-differences analyses on mortality rates of 15-19 and 20-24 year olds for all of the external causes listed above.  Those were the only age groups publicly available through CDC's WONDER database, and while not ideal, taken together they are still useful for generating estimates of the net effects in the long run, which we did.  The control group was the 11 states (excluding Utah) that did not change their drinking ages (i.e. they remained 21 throughout since the 1930s and 1940s), while the treatment group was the states that had a drinking age of 18 in 1979 and later raised it to 21.  Comparing 1998 to 1979, we found that the net difference-in-differences between the groups had the "wrong" sign for nearly every cause of death, especially suicide for 15-19 year olds.  Only for homicide was there an apparent lifesaving effect, but removing New York from the data attenuated this effect to almost null.  The pattern for suicide vs. homicide appears to be the reverse of what Carpenter and Dobkin found.  Overall, we found no net lifesaving effect in the long run, echoing what Miron and Tetelbaum found for traffic deaths, and thus perhaps Carpenter and Dobkin's results are primarily capturing short-term effects due to the study design.

Next, the study's authors discuss their previous work on regression discontinuity estimates using more recent data, which we critique here.  This analysis shows a discrete and significant jump in mortality at exactly age 21.  The effect is true only for external causes of death, including motor vehicle accidents, suicides, deaths labled as "alcohol related," and those labeled as "other external," but not homicides or drug-related deaths.  Another similar study they did concerning various types of crime gave similar results overall.  But unfortunately, they also make the specious claim that such an effect is not merely a delay in deaths, but rather constitutes a true lifesaving effect of the policy (which is dubious).  In any case, it certainly shows once and for all that there is nothing at all about turning 21 that magically makes one a safe responsible drinker.

The authors then tie together all of their analyses thus far, and assert that despite all of these limitations, the similarity of the effect size (8-10%) between the regression discontinuity analyses and the panel estimates implies that the effects of the 21 drinking age are likely to be truly causal rather than a proxy for something else.  We find that argument to be puzzling at best, especially since Miron and Tetelbaum also found a similar effect of MLDA-21 (8-11%) in their initial 50-state model relative to MLDA-18, but it nonetheless dropped well below statistical and practical significance when the states were disaggregated and when the persistence of the effect was analyzed.  For some states, it apparently even made things worse.  Thus, an effect of this size may very well be a mirage rather than a truly causal relationship.

But the most tenuous aspect of the author's latest study is their analysis of the "social costs" in dollars per drink consumed by people under 21 if such drinking was legalized.  Not only do they presume that the effects they observed in the aforementioned analyses are causal and represent a net lifesaving effect of the 21 drinking age, which we doubt, they also leave out much of the other side of the ledger with respect to alcohol consumption by ignoring or dismissing several potential economic benefits associated with it.  They also ignore the likely adverse effects of a high drinking age on social cohesion, as well as the fact that forcing alcohol use underground makes it far more dangerous than it has to be, to say nothing of the value of individual liberty.  And the by the same measures, the social cost per drink would likely be at least as high for people over 21 on balance, especially 21-24 year olds who are the most likely of any age group to drive drunk (both in the USA as well as countries with lower drinking ages).  Using their logic, even bringing back Prohibition could potentially be justified, and we all know how well that worked out. 

On balance, the 21 drinking age is an EPIC FAIL.  And even more so are the tired, old attempts to justify it.


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