Five Studies that Debunk the Rest

Over a hundred studies have been done on the effects of the drinking age, mainly on traffic fatalities. The pro-21 crowd claims that "science" is entirely on their side. However, about half of the studies done suggest otherwise. The best they can honestly say is that the jury is still out. The majority of drinking age studies are either cross-sectional in design or look at time-series data in only one state (or province). Not all studies control for potentially confounding variables or even have a comparison group. A few good ones do, and some of those still find a lifesaving effect for a higher drinking age, but no study is perfect, and there are always unmeasurable variables that are left out due to lack of data. Other problems include the definition of "alcohol-related," poor and widely varying alcohol testing rates, the non-existence of the FARS database before 1975, and policy endogeneity. Even the relatively good studies in favor of a high drinking age can be readily debunked with no more than five other studies, the ones that the pro-21 crowd doesn't want you to see. Consider these studies to be pieces of a puzzle; while they (like all studies) each have their own strengths and weaknesses, they fit together quite well as the strengths of some compensate for the weaknesses of others.

The Furious Five

The five studies that debunk the rest, in chronological order, are:

Males (1986)
Asch and Levy (1987)
Asch and Levy (1990)
Dee and Evans (2001)
Miron and Tetelbaum (2009)

1) Asch and Levy found in their first study that the drinking age had no significant (or even perceptible) effect on either 18-20 year old traffic fatalities or all-ages fatalities, even when single-vehicle nighttime crashes (a proxy for alcohol-involvement) were studied.  It also found no evidence of endogeneity in a state choosing on a lower drinking age. The strengths of this study were that it controlled for several variables, used an error term in the regression, and is one of the few studies that controlled for adult per capita alcohol consumption. The one weakness was that this study was cross-sectional in design and looked only at the year 1978. However, this year was chosen on purpose because all of the drinking age lowering from the early 1970s had occurred years ago, and only a few states had recently raised the drinking age.  In short: the Asch and Levy study was designed to check for long-term effects of the drinking age. It found none.

Interestingly, a 1984 study by Israel Colon did a similar cross-sectional study for the year 1976, and found a positive correlation between the number of single-vehicle fatalities and the drinking age (higher drinking age = more deaths).  The author attributed it to border effects from neighboring states with lower drinking ages (similar to the case of dry counties adjacent to wet ones), but the Asch and Levy study (which controlled for more variables than the Colon one) found no difference in their own results when they eliminated all states for which border effects were potentially important from their regressions.

2) Their second study, longitudinal from 1975-1984, did not show a very conclusive relationship between drinking age and fatality rates. The drinking age oddly enough had opposite effects on single-vehicle (SV) versus single vehicle nighttime fatalities (SVNT). Effects on former had the expected sign, while the latter the effects were statistically insignificant and even had the "wrong" sign. It did, however, show significant effects for experience drinking legally, independent of the drinking age, which greatly diminished the drinking age effect on SV fatalities (often to nonsignificance) and strengthened the wrong-signed effect SVNT fatalites even more in the opposite direction. The more experience, the fewer traffic deaths. Thus, if the drinking age did have any effect, which was still left uncertain, it was mainly to postpone fatalities by 1-3 years rather than cause a net reduction. Strengths were its longitudinal design and inclusion of both state and year "fixed effects," which controlled for state-specific characteristics that did not change significantly with time, and national trends, respectively. The only weakness was the very small number of other control variables in the regressions, but additional ones that were tested (such as the 25-29 year old fatality rate) did not substantively affect the results and were thus dropped for the sake of parsimony.

3) Dee and Evans, using data from 1977-1992, found that, after controlling for several confounders and fixed effects, a drinking age of 21 did reduce fatalities slightly for 18-19 year olds, but increased them for 22-24 year olds, merely shifting the deaths a few years into the future. In other words, no net lifesaving effect, and possibly even a net increase in fatalities. Effects on 16-17 year olds were less clear; a drinking age of 18 (relative to 21) apparently reduced fatalities in this group while a drinking age of 19 increased them. Strengths were its longitudinal design, state and year fixed effects, a few control variables, and the fact that 16-17 year olds and 22-24 year olds were included. The time lag for the effect on 22-24 year olds was taken into account, unlike most other studies that looked at this age group. The only major weakness was not including data for 20 and 21 year olds, especially the latter, which makes the net effect on fatalities less clear (since some other studies suggest a spurt in traffic fatalities at age 21). However, if anything, this omission would attenuate the fatality increase for 21-24 year olds.

4) Mike Males got similar results more than a decade prior, using different methodology and data from 1976-1983, finding that there is not only a "seesaw effect" between age groups regardless of what the drinking age is, but a higher age generally leads to a net increase in fatalities overall. The TSAP speculates that the longer the drunk drivers live, the more of a chance of killing others in a crash. The study compared the changes in the fatal crash ratio (relative to 21-24 year olds) of 18, 19, 20, and 21 year olds in several "change" and "no-change" states that were matched based on various similarities. His methodology has been sharply criticized by many in the pro-21 crowd, but it was not radically different from that used in a pro-21 study by the Insurance Institute for Highway Safety, and actually used more statistically reliable measurements.


5) But the final nail in the coffin comes from a study done in 2007 (and published in 2009). Miron and Tetelbaum (2009) found that, after controlling for numerous confounders and fixed effects, as well as state-specific trends, only the first few states to raise the drinking age to 21 voluntarily saw any statistically significant reduction in 18-20 year old fatalities, while many of the coerced adopters saw no change or even increases. And even for the early adopters, there was an apparent rebound effect after the first two years of the higher drinking age. Again, no net lifesaving effect in the long run. They found no statistically significant effects on those over 21, but that could be due to an unaccounted for time lag (when the first 18-19 year olds exposed to a drinking age of 21 turned 21 2-3 years later).

But what about high school kids? Contrary to popular opinion, Miron and Tetelbaum also found little to no effect of the drinking age on reported high school drinking (in Monitoring the Future survey data) as well after controlling for several confounders, and such effects are consistent with underreporting. Even these weak effects were not robust to a change in model specification that restricted the sample to states that raised the drinking age in response to federal coercion. It appears that they are willing to drink regardless, and that the drinking age is irrelevant or even counterproductive. In fact, they found that the higher the drinking age, the more 17 year old (and under) driver fatalities there were! That "negative spillover" effect was also somewhat consistent with Dee and Evans (2001), though it was less clear in the latter.

Most of Miron's statistical models were slightly modified versions of a model used by Dee (1999), in which lifesaving effects were found for the 21 drinking age, but no lifesaving effects were found for the beer tax (in fact they had the "wrong" sign). This is important because Dee (1999) was (until recently) the virtual gold standard for the pro-21 studies as it was a longitudinal study that controlled for several potential confounders, fixed effects, and even state-specific trends. Miron simply took Dee's best model from 1999 and a) added Alaska, Hawaii, and DC to the data, b) added vehicle miles traveled (VMT) and BAC limit variables to the regressions, and c) compared the effects of including or omitting the first few states that raised the age to 21. The drinking age effects were somewhat diminished with the second change and not at all robust to the third change.

Interestingly, the mere addition of Alaska and Hawaii (two of the highest beer tax states) and DC to Dee's best 1999 model made the beer tax suddenly become significant (at the 10% level) and have the correct sign, a drastic change from Dee's results. That is probably because the lower 48 states (except Alabama) and DC have much lower beer taxes (often an order of magnitude lower). It was also worth noting that, in the model that was identical to Dee's except for including AK, HI, and DC, the effect of doubling the beer tax had about twice the apparent effect that raising the drinking age from 18 to 21 did. And that was before the model was changed further in ways to which the drinking age effects were not robust.

QED

Post-Miron Studies

The aforementioned studies do an excellent job of debunking all the pro-21 studies done prior to 2007. A few more studies have been done since then, and it is now up to us to debunk them:

1) Even in some of the studies that do suggest lifesaving effects of a high drinking age, we also learn that the beer tax potentially has a lifesaving effect as well. For example, Ponicki et al. (2007) even found that, while the drinking age does have a small effect, there is a negative "interaction" between the drinking age and the beer tax: the higher one is, the less effective the other is in reducing fatalities. Their model suggested that if the beer tax is high enough, the drinking age becomes irrelevant or even counterproductive. While the study controlled for more variables than most, as well as state and year fixed effects, it did not control for state-specific trends like Miron and Tetelbaum (2009) did. It is also important to note that this study did not adequately test the conclusions made by Miron and Tetelbaum (2009) or Dee and Evans (2001).

2) Lovenheim and Slemrod (2010) also came out with a recent study that looked at the effects of the drinking age itself, as well as "blood borders" (effects of unequal drinking ages across neighboring states). They apparently found small but statistically significant lifesaving effects of a higher drinking age, but the opposite was true in counties within 25 miles of a lower drinking age jurisdiction, for obvious reasons. They imply that if some states were to lower the drinking age, they would hurt others due to drunk driving across borders. That was one excuse the feds gave for their power grab in 1984. Nevermind that the exact same thing happens in dry counties among those 21+, as verified by some studies (Baughman et al., 2001), and yet we do not say that wet counties "hurt" their dry neighbors. Rather, we say that the dry counties are hurting themselves with their provincial and unenforceable policies, and we let them take the consequences of those policies. Futhermore not every study agrees with their conclusion about border effects, such as Kreft and Epling (2007), who found no robust border effects in Michigan counties that bordered on areas with lower drinking ages (Wisconsin, Ohio, and Ontario) back in the 1980s.

The authors were familiar with Miron and Teltelbaum (2009), and even reference that groundbreaking study. Lovenheim and Slemrod's study was very different from the latter, however. Not only was it one of the few studies that looked at border effects in great depth, it also had different methodology. Their fatality measure was the ratio of 18, 19, and 20 year old driver fatalities, analyzed separately, relative to those of 21-25 year olds in one model, and 26+ in another. Two models were done for each, one including border effects, and the other neglecting it. Border effects were localized to those counties 25 miles from the border of a lower drinking age jurisdiction, and were essentially exclusive to the higher drinking age side (similar to what happens dry counties when the drinker drives out sober but drives back home drunk).

However, there are several flaws and caveats. The authors imply that Miron was refuted since Lovenheim still found effects post-1984, but they only restricted the time period studied, not which states were included like Miron did. In fact, they strangely did not even look at what separating out early-adopting (i.e. non-coerced) states would do to the results, even though the gist of Miron was to do exactly that. While Lovenheim and Slemrod point out that most states had drinking ages of 19 or higher by 1984, and that lumping 18-20 year olds together may therefore distort the data, they fail to mention that Miron tests the specific effects of MLDA19, MLDA20, and MLDA21 relative to MLDA18, and there were still some states that were 18 until 1987. So this is essentially a non-issue. Effects of the drinking age were robust to neglecting border effects, and in fact roughly identical in both models, so Miron's neglect of border effects was also not substantive.

Most importantly, Lovenheim's models using 21-25 and 26+ control groups differed in terms of drinking age effects, and the differences are very telling indeed. The effect of drinking age on fatality rates of 18-19 year olds was twice as strong in magnitude when the 21-25 control group was used compared with using 26+. For 20 year olds, the difference was smaller but still visible. Hmmm...how could that be? Though glossed over, a stronger relative effect with respect to 21-25 year olds than with 26+ year olds implies that some (if not all) of the reduced 18-20 year old traffic deaths were likely just postponed by a few years, Dee and Evans (or Asch and Levy) style. A true net reduction should not have such differential effects. This possibility was unfortunately ignored by the authors, so the net effect is still unclear in this study. Thus Lovenheim and Slemrod fail to knock down the aforementioned studies.

Finally, it is rather interesting that border effects involving the Canadian border were found to have the opposite sign compared with those of state borders. This led the authors to admit (in a roundabout way) that the counties in upstate New York and Vermont, which were known to beef up roving patrols and sobriety checkpoints close to the Canadian border at a time when the border was not much more protected than state borders, found a way to more than counteract the apparent border effects. Put another way, this actually pulls the rug out from under the strongest argument for states being coerced to have a uniform drinking age of 21. States who refuse to recognize 18-20 year olds as full adults, but whose neighbors are intent on doing just that, take note. It just might save some lives.

3) Fell et al. (2008) also came out with a recent pro-21 study, and it has been hailed by some as the one study that was finally able to tease out the effect of the drinking age alone, and settle the debate once and for all. Red flag statements aside, this study by MADD member James Fell still suffered from some serious issues. The study was divided into two parts. The first part looked at the effect of the drinking age from 1982-1990, using the ratio of alcohol-positive to alcohol-negative fatal-crash under-21 drivers as the fatality variable. States with a drinking age of 21 since before 1982 were compared with states that did not. While modest but statistically significant effects were found, even when numerous variables were controlled for, there are some caveats that were glossed over. First, the apparent convergence of the fatality ratios in the two groups did not occur until 1988, with the gap persisting even in 1987, even though most of the age-raising occurred in 1984-1986, and only a handful of states changed ages in 1987-1988. Until 1988, the ratios declined at roughly the same rate, albeit a gap between them that persisted until then. The gap should have begun narrowing since 1984 if the drinking age effects were real. In fact, in 1990, re-divergence began despite no change in drinking age after 1988, and the percent change from 1982-1990 was not dramatically different between groups.  Secondly, the effects of a 0.08 BAC limit and automatic license revocation laws had much stronger magnitudes than those of the 21 drinking age. Thirdly, alcohol testing rates were abysmal and erratic before 1990, which could bias the results in either direction. Remember too that "alcohol-positive" means any alcohol (even 0.01 BAC) was present in the driver's body, not necessarily that the crash was alcohol-caused. Fourthly, beer taxes and seat belt laws were not controlled for. And finally, it goes without saying that since it did not compare the post 1984 change states to the early MLDA 21 adopters between 1982-1984, it does not successfuly refute (or even address) Miron and Tetelbaum's findings. Also, it does not even broach the issue of shifting deaths to 21-24 year olds, so it does not refute Males, Asch and Levy, or Dee and Evans.

The second part of Fell's study is sometimes hailed as a strong point in that it includes "modern" data, but upon closer examination it actually contains the study's deepest weakness. It looks at the same under-21 alcohol-related fatality ratio as above, only this time as a percentage of all-ages fatalities, over the period 1998-2004. The effects of the two "core" drinking age laws (purchase and possession under 21) and 14 ancillary laws (anti-fake ID, keg registration, furnishing to minors, social host laws, graduated driver licensing with nighttime restrictions, zero tolerance, use and lose, and others), and the relative "strengths" of those laws, on fatalities was examined. The only one that had any significant and negative effect on under-21 fatalities, relative to over-21 fatalities, was the anti-fake ID law, a law that all 50 states have had since before 1998 but varied in strength from state to state. All of the other laws, even the two core laws, were either insignificant or even perverse, calling into question whether these or even the 21 drinking age itself is still useful or relevant today. Since drivers under 18 were included in the under 21 group, the fake ID law's small effect could very well have been driven by such youth since they would be just as affected by this kind of law if not more so. Or it could simply be a proxy for something else that was not observable (the same could also be said for the drinking age itself, by the way). The authors try to explain away the apparently null or perverse effects of the other laws by the way the "strengths" were coded as well as the fact that this part of the study was cross-sectional due to data problems for enactment dates, but one can just as easily make the exact same argument about the fake ID laws as well. Far from settling the issue, this study acutally opens up a huge can of worms. So consider this one debunked as well. The bigger they are, the harder they Fell.

UPDATE:  Fell et al. (2009) also did another, more recent study that looked this time at both the 21 drinking age as well as a few ancillary laws (zero tolerance, use and lose, graduated driver license night restrictions, and keg registration) that were evaluated longitudinally, in contrast to their 2008 largely cross-sectional evaluation of ancillary laws that found no significant effects for laws other than anti-fake ID laws.  Their longitudinal study did find a significant downward effect of the "core" 21 drinking age laws and smaller but statistically significant effects of use and lose laws and zero tolerance laws on the ratio of alcohol-related to non-alcohol traffic fatalities among 16-20 year olds, but keg registration unexpectedly had the opposite effect, acutally increasing this ratio.  That result is surprising since outdoor keggers frequently involve at least someone driving when they shouldn't be on the road.  Thus, if one believes the study's conclusion that the 21 drinking age and use and lose laws both save hundreds of lives each year, you'd also have to believe that keg laws kill people as well, and that their proponents have blood on their hands.  In addition, though the model was somewhat improved, the study still suffers from many of the same shortcomings as the authors' previous study, and cannot be said to truly refute Miron and Tetelbaum and the other Furious Five studes.

QED