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Did liberalising abortion reduce US crime?

In relation to the post immediately following, Rabee Touky provides a link to C.L. Foote and C.F. Goetz ‘ Testing Economic Hypotheses with State‐Level Data: A Comment on Donohue and Levitt (2001)’ here which critiques the conclusions of J.J. Donohue and S. D. Levitt ‘The Impact of Legalized Abortion on Crime’, Quarterly Journal of Economics, 116:2, pp. 379–420′ (an unpublished version here). They claim there is a significant error of reasoning. Correcting for this error Foote and Goetz claim there is no evidence that liberalising abortion laws led to a decline in US crime rates.

In response, Donohue and Levitt in, “Measurement Error, Legalized Abortion, the Decline in Crime: A Response to Foote and Goetz (2005), (here) acknowledge the error but claim that, correcting for it, leaves their original conclusions intact. They argue that liberalised abortion laws explain about half the reduction in US crime rates.

There is an animated discussion on this debate over at the Freakonomics blogsite. The issue is also discussed in The Economist here. In my view Foote and Goetz have a point. My brief response is as follows:

FG criticism. DL claim that higher abortion rates mean less crime. This is partly because crime rates are concentrated among young age groups but also because, DL claim, unwanted children are more likely to be criminals. FG denies evidence for this second link although they agree the first link will operate.

DL test the abortion crime link by comparing criminal behaviour of different groups of young people. These groups are defined by their birth years and state of residence. These groups will have different ‘abortion exposures’. They test if those with a high exposure are less likely to commit crime. The difficulty is that different states will be exposed to other differences in factors that might motivate criminal behaviour – for example the introduction of crack cocaine. If these specific state-year factors affect states at the same time as changed abortion laws, but are not controlled for, they will distort conclusions relating to links between abortion and crime. In DL’s case controls can be used because DL has several points within each state-year combination based on abortion exposure for different age groups (15 year olds, 16 year olds etc). Then one can calculate the difference between the original age specific data and the average abortion exposure and average criminal activity within each state and year to eliminate any factors that affect all ages within a state equally. Then look at the relation between demeaned crime and demeaned abortion exposure.

One could also control for state-year effects that operate on the age-year level or the state-age level. An age-year factor would affect all US individuals of a certain age while a state-age factor would operate if people of different ages in different states were more likely to commit crime. Eliminating state-year, age-year and state age effects would allow a test of the hypothesis that abortion exposure drives crime. This can be achieved by regressing arrests (in a particular year, with a cohort born in a particular state with a particular birth year) on abortion exposure in that state and for that birth year along with state-year controls. DL didn’t include this latter variable.

FG also criticise DL on the more basic grounds that when comparing arrest propensities they use total arrests not arrests per capita. This confuses things because it will mix up reduced crime from the first channel (less potential criminals) with that of the second channel (less unwanted children).

FG do this and recompute DL regressions with controls and with variables in per capita terms and find that abortion exposure has a statistically insignificant effect on per capita arrest rates once state-year controls are accounted for. Abortion would only operate to reduce crime by reducing numbers in young age groups who commit crime.

DL counterargument. DL respond that their earlier paper provides six types of evidence that abortion exposure reduces crime and that the FG critique influences only one of these types of evidence. They point out that the insignificance results of FG only arises when state-year effects are accounted for and when ‘arrests’ are replaced with ‘arrests per capita’. They claim is this finding is an artifact of using a crude abortion proxy – indeed the proxy that they used in their original paper. They come up with a new measure that (i) accounts for the actual month and year of birth of an individual; (ii) incorporates cross-state mobility between birth and adolescence and (iii) reflects the state of residence of those having abortions – to account for the fact that women crossed state lines to get abortions. Correcting for measurement errors and allowing for state-year interactions – but not expressing arrests in per capita terms and hence not accounting for the first channel of influence of abortion on crime – increases the significance of the abortion impact on crime. DL then account for population level impacts by including an explanatory population variable and by expressing violent arrest rates in per capita terms. Then impacts of abortion are reduced presumably because the first channel of influence is accounted for – indeed DL claim 40% of the influence occurs via this channel. For property crime arrest rates the results linking abortion to crime are weaker and statistically significant only when an instrumental variable (measuring abortions by place of occurrence rather than state of residence) replaces the adjusted abortion variable.

Verdict. The FG criticisms are valid and the original paper by DL is flawed. There are problems when state-year interactions and population level effects are accounted for. Changing the variable used to measure ‘abortion exposure’ restores the DL conclusions when population level effects are not incorporated but substantially reduces their effects on violent crime rates when it is included – 40% of the reduction in crime occurs not because of ‘unwanted babies’ but simply because there are fewer individuals around who will commit crimes. On property crime rates, the earlier results are restored only if a proxy is included for abortion exposure which measures abortions by place of occurrence rather than residence – curiously this is one of the defects that DL recognise in their original data set. Even accepting the DL data revisions the impact of abortion on crime is lower than originally envisaged.
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