I've just received the book, Climate Change in Prehistory: The End of the Reign of Chaos, by William Burroughs. I'll be reading it and reviewing it during the next couple of weeks.
For the time being, I found a short passage of the book's introduction that helped me to put into words something I've been thinking about this week.
Before this passage, Burroughs has described the sources of new evidence about climate and its effects on humans in the past. One of these areas is genetics, in particular the emergence of mtDNA and Y chromosome haplotypes as markers relevant to ancient migrations. The other is Greenland and Antarctic ice cores, which by 2004 had allowed course-scale temperature reconstructions over the last 800,000 years or so.
After these, he discusses archaeology -- what we might usually consider to be the most direct source of information about humans in the past. But as Burroughs describes the situation, the relevance of archaeology is somehow fundamentally more difficult to describe:
It is often easier to write with confidence on fast-developing and relatively new areas of research, such as climate change and genetic mapping, than to review the implications of such new developments for a mature discipline like archaeology. Because the latter consists of an immensely complicated edifice that has been built up over a long time by the painstaking accumulation of fragmentary evidence from a vast array of sources, it is hard to define those aspects of the subject that are most affected by results obtained in a completely different discipline. Furthermore, when it comes to many aspects of prehistory, the field is full of controversy, into which the new data are not easily introduced. As a consequence, there is an inevitable tendency to gloss over these pitfalls and rely on secondary or even tertiary literature to provide an accessible backdrop against which new developments can be more easily projected (Burroughs 2005:10).
I think this is a revealing quote. From the standpoint of someone describing an emerging science, as Burroughs is doing in the book, there must be intense frustration. It seems so simple when you compare climate data and genetic data. Humans underwent some catastrophic population declines in the past, and there were big climate fluctuations. What could be simpler? But then, you get to the archaeological record where nothing is simple at all.
Imagine the author had written the paragraph above as an exercise in self-reflection. Either of two things might logically follow:
1. ... and therefore the simple conclusions of the immature sciences may be wrong.
2. ... and therefore those wishy-washy archaeologists had better get their act together.
I won't prejudge which of these Burroughs comes to -- for that, I'll need to review the rest of the book. But you can see the temptation to arrive at the second -- the supposedly "mature" science is hopelessly mired in meaningless debates. The new sciences of genetics and climate change will finally bring simplicity and allow a new revolution of archaeological insight.
I'd like to write a few words in favor of maturity.
What marks a "mature" discipline is the emergence of informed critiques focused on the limits of methods of analysis. When archaeology was immature, before the 1950s or so, almost all archaeologists were simple (some say "naive") positivists. They excavated and found the traces of ancient people, just as today's archaeologists do. And what they found was what there must have been. Find a handaxe, you know people made handaxes; find a temple, you know they worshipped gods of some kind. Dig in a mound, find a grave, you know that the people had rituals associated with death that required substantial non-subsistence directed labor.
Of course, today's archaeologists tend to be positivists, too. There's no sense twiddling around with hypotheses that will never be testable. The religion of Neandertals? Well, it's one thing to speculate about it, but the fact is that it's devilishly hard to test hypotheses about religion from the material remains of any pre-monumental culture. In the absence of information, we may as well stick to the facts.
But there's a deeper sense in which archaeologists have a much more complicated view of their evidence. Archaeology has gone through many periods where different researchers developed and applied distinctive analytical techniques. These techniques have often been incommensurable. Sometimes they settle debates. For example, the systematic study of skeletal element representation and cutmark taphonomy has gone far toward testing (and verifying) the occurrence of hunting in some Early Pleistocene contexts. The hunting versus scavenging debate still goes on, with renewed emphasis on active or confrontational scavenging. But knowledge advanced by means of analytical critique.
These kinds of internal critique have fueled many of the great debates in archaeology. For example, the technical standardization promoted by François Bordes enabled a new kind of systematic comparison of assemblages with each other. But those new data gave rise to several vociferous differences of interpretation. Where Bordes had favored a cultural interpretation of site differences, Lewis Binford critiqued the emerging pattern along functional lines. Later Harold Dibble and others critiqued the stability of artifact types, noting the emergence of some categories as side effects of the reduction sequence. These critiques did not lead to any quick resolutions, but they allowed archaeologists to deepen our understanding of the cognitive and functional circumstances of artifact production and transmission. They taught us the limits of comparison by showing the weakness of particular artifact types as markers of cultures.
In human genetics, we have the assumption that particular haplotypes are markers of populations. Critiques of that assumption go back more than fifteen years, but I think it fair to say that they have not taken hold. It's worth asking, "Why not?" Why does a tradition of effective critique emerge in some areas of science but not others?
A large part of the answer is the culture of practice in human evolutionary genetics. Let me give an example. Last week, I had my students read a selection of review papers published this month in Current Biology. I mentioned those papers here a couple of weeks ago ("Genes and archaeology"). These papers are reviews of the basic findings of genetics as applied to the last 50,000 years of evolution in most of the major regions of the world.
Toward the end of our session, I asked, "What methods did you find unifying this set of papers?" That is, what basic methodology do they have in common?
The students really couldn't find any shared methodology, beyond a few issues strongly connected to the data. For example, there was a shared reliance in most of the papers on the two uniparentally inherited gene systems -- mtDNA and the Y chromosome. Several of the papers came down to issues regarding the exact mtDNA chronology, and none of them seemed to deal seriously with the discrepancies between mtDNA and Y chromosome timescales. But when it came to methods of analysis -- how do we go from genotypes and haplotypes to some knowledge that populations had a particular history -- the papers had no systematic way of answering those questions.
The demographic models developed to test hypotheses about human evolution are different in almost every study of human genetic variation. Since our evolutionary history has been complicated, simple mathematical models won't often be very effective tests of events in our evolution. So we need to apply simulation modeling of various kinds.
The necessary computer programs tend to be written by graduate students and postdocs. Principal investigators -- the scientists in charge of the lab -- are rarely directly involved in this kind of work in human genetics, although there are exceptions. The development of distinctive simulation methods in many different labs raises important issues about replicability and code quality -- some students document their code well and have extensive backgrounds in computer programming, but most do not. This situation is terrible from the standpoint of developing a shared analytical methodology -- when the students leave the lab, or when the dataset changes, the next group of students and postdocs usually ends up developing new methods.
Some groups work with standardized simulation code that has published documentation. But the students and postdocs apply distinctive parameters that rarely match those used by other research groups. That is, the programs may be standard, but the parameters are idiosyncratic. Maybe they choose parameters that provide the best fit to a particular dataset. Or maybe they choose them through a set of discussions at the laboratory level. In any event, when the data change, and when the students and postdocs change, the models change.
That means the results of different studies may be incommensurable, even if they look the same. A reviewer who just reads the conclusions of such analyses may think that they are all consistent with the same story -- even though the simulations in one paper actually may contradict the results of other papers. Papers appear unified at the level of conclusions, but not by virtue of having a shared system of methods.
Now, what does archaeology have to do with this? Well, in the case of human evolution, we have an archaeological record. It would be sensible for archaeologists to contribute to the project of genetic modeling and simulation methods -- that way, we would be testing models that could be critiqued on the basis of archaeological reality as well as genetics. But the students and postdocs who develop simulation models in genetics don't know archaeology. And most of the archaeologists don't know genetics -- so they discuss models only at the level of conclusions, not at the level of parameters.
The tradition in archaeology for the last fifty years has supported the devleopment of robust critiques. Likewise, the tradition in evolutionary genetics has supported such developments -- witness the rise of neutral theory, the "selfish gene" revolution, the innovation of evolutionary game theory. Each of these involved the discovery of weaknesses in old population models, based in part on a growing program of empirical research on natural populations and mathematical models.
I don't want to push this comparison beyond reason. There is a point of overcaution -- of superfluous critique that can impede progress. Archaeologists have beached themselves on the shoals of such critiques many times.
But human evolutionary genetics remains immature. We should be cautious about the details of population models, and we should try to identify lines of critique that will improve them. Some critiques have begun to emerge, and I will be highlighting those over the next several weeks in my course. In addition, I'll be discussing some lines of inquiry based on open access datasets that will illustrate problems in recent human evolution, along with some potentially productive approaches for solving them.