Two days ago, Nature published a review article by Terrie Moffitt that “recaps the 25-year history of the developmental taxonomy of antisocial behaviour, concluding that it is standing the test of time…”
It should also be mentioned that the taxonomy has received quite a bit of criticism (which are not mentioned in Moffitt’s review), and I feel that also much of this critique is standing the test of time. It would have been a good thing if the 25th anniversary of the taxonomy took the time to clear up some misunderstandings, controversies, and make some clarifications. However, Moffitt refrains from doing so, and I am not so sure the debate has moved forward. I have made some contributions to this debate, and I think my points are as relevant as ever. See here and here. It feels a bit wrong that they too stand the test of time. Importantly, so does the critique made by others.
In her recent review, she repeats what she also claimed in her 2006-review of evidence: a very large and important part of the empirical evidence supporting her theory is from studies using this latent trajectory models which. A key piece of evidence seems to be the identification of the hypothesized groups, as she states: “Since the advent of group-based trajectory modelling methods, the existence of trajectory groups fitting the LCP and AL taxonomy has now been confirmed by reviews of more than 100 longitudinal studies”. The method is a particular kind of latent class model for panel data. I would say this evidence is pretty weak. First of all, my discussion of trajectory models makes it clear that seemingly distinct groups can be detected in data where there are none. Since the further test of hypotheses relies on the identification of groups, these hypotheses are not reliable evidence either. The empirical evidence for the taxonomy is thus equally consistent with competing theories, and thus at best very weak evidence for either. Others have made similar points as well.
In her new article on page 4 she makes the claim group-based trajectory methods are capable of detecting hypothesized groups. The method does no such thing. It is a data reduction technique, which might be convenient for some purposes but it does not detect distinct groups. It creates some clusters, but it could equally well reflect an underlying continuous reality. Moreover, that the existence of these groups is confirmed across studies is so only if one accepts pretty much any evidence of heterogeneity in individual trajectories. As I pointed out in an article from 2009, the findings across studies are so divergent except that there is some kind of high-rate and low-rate groups, that it is hard to imagine any results from trajectory modelling that would not be taken in support of the taxonomy.
In short: At the best, the empirical evidence is consistent with the taxonomy. But this is largely uninformative as long as it is also consistent with pretty much all competing theories that acknowledge that different people behaves differently. The bottom line is that there are no evidence that there are qualitative differences between the “groups” (at least no such evidence are presented in Moffitt’s recent review). There might be quantitative differences, though.
The other risk factors she discusses and its relation to the groups could just as well be interpreted as differences in degree. However, on page 5, she dismisses that there might be quantitative rather than qualitative differences! (This is the closest to a clarification of whether she actually means literally distinct groups or not). Now, the evidence I have seen so far, shows that there are indeed differences between the average scores in the two groups, but most theories of criminal behaviour would expect higher scores on all risk factors for the highest-offending persons. While it sounds great that she proposed hypothesis in her 1993-article that have later proved correct – these hypothesis are also very general and consistent with other perspectives.
The key point here is that the empirical evidence is consistent with the taxonomy – and pretty much all other theories. It seems that the theory has not been put to a strict test in these 25 years. In a previous post, I made the following argument which holds generally:
I think (but I am not entirely sure), that in this context “testing a theory” only means findings that are consistent with a given theory. I think this is a generous use of the term “test”. I prefer to reserve the word “test” for situations where something is ruled out – or when using methods that at least in principle would be able to rule something out. In other words: If the findings are consistent with a theory but also consistent with one or several competing (or non-competing) theories, this is at best weak evidence for either theory. (This holds regardless of methods used). It is good that a theory is consistent with the empirical findings, but that is far from enough.
Second, in 2009 I wrote a more theoretical paper assessing the arguments in the taxonomic theory. A major point was that no argument are presented that there are distinct groups in the first place. However, one might argue that I have interpreted the theory too literally regarding the distinctness etc, so in this article, I also make an explicit discussion of this possibility. In 2009, I argued that since there are clearly some confusion regarding this issue, it would have been reasonable if someone (preferably Moffitt, of course) clarified if she really meant distinct groups or not. I am not aware any such clarification to date. But, as mentioned, she now goes a long way on dismissing the differences in degree interpretation (see her new article on page 5). I think the argument made by Sampson and Laub still holds: if LCP is just another term for high-rate, then the theory brings nothing new to the table. Indeed, all the mechanisms and risk-factors discussed are relevant and sound, but does not at all rely on a taxonomy as such.
In my view, the review should have concluded something like this: First, while much empirical evidence is consistent with the taxonomy, there is a lack of good evidence for the existence of groups. Second, there are still theoretical arguments that are unclear and needs specifications to allow for strict empirical tests. Nevertheless, the taxonomy has helped focusing on some important risk factors and mechanisms. (Although these factors were also known in 1993 according to Moffitt). Whether the taxonomy itself is needed to do so is less clear. Important work remains to be done.
What I am saying in some elaborate way is that the standards for what counts as empirical evidence in support of a hypothesis is too low. So is the precision level for “theories”. I know it is hard, but we should be able to do better.
PS Moffitt also refers to one of my articles on her first page when stating that “Chronic offenders are a subset of the 30–40% of males convicted of non-traffic crimes in developed nations”. My article says nothing of the kind, but tries to estimate how many will be convicted during their lifetime. It is just the wrong reference, but would of course recommend reading it 🙂
PPS I take the opportunity to also point out that while Nagin has previously claimed that my critique is simply based on a fundamental misunderstanding of his argument (see my comment on Nagin here), I have always argued, regardless of his position, that my methodological arguments are important because of how others – like Moffitt has just demonstrated – misunderstand the methods and the empirical results. Nagin also has a responsibility to clarify such prevalent misunderstandings.
The post Moffitt review her own theory appeared on The Grumpy Criminologist 2018-02-26 20:47:05 by Torbjørn.