Guest blogger Douglas H. Erwin writes...
One of the joys, and benefits, of getting older is that one begins to indulge oneself a bit more. You begin to worry a bit less about reputation, or how many people (if any) will read the paper you have spent months working on, and take up projects just because they seem interesting. In my case, one of these projects has been indulging more in my interests in the history and philosophy of the historical sciences – mostly paleontology and evolutionary biology, but with the occasional look-in at other fields such as archaeology.
In truth, my interests in this area date to my time as an undergraduate at Colgate University, where I took a January-term course in Philosophy of Science, and spent much of my senior year in independent study courses with my advisor, Bob Linsley. (Bob was one of the great undergraduate paleontology teachers of all time, with, I think, about 25 of his students going on to Ph.Ds in paleontology or biology. A remarkable record from a small school like Colgate).
But I have been troubled by what I see as an over-emphasis on philosophical issues associated with the work of Stephen Jay Gould. Gould’s all-too-early death in 2002 was a terrible loss for the field: Steve made important and significant research contributions beginning as a graduate student, was an enthusiastic communicator of scientific ideas to a broad public audience, and enjoyed his role as a public intellectual (perhaps culminating in his ‘appearance’ on The Simpsons). Many of Steve’s contributions have received considerable scrutiny from philosophers, from his early contributions in Ontogeny and Phylogeny (1977) to the punctuated equilibria debates generated by his papers with Niles Eldredge and the subsequent controversy over species selection. The Spandrels of San Marco paper with Dick Lewontin sparked considerable interest, and of course Gould’s claim in Wonderful Life for the ubiquity of contingency as a factor in the history of life continues to resonate. Gould clearly dealt with some important conceptual issues, but I think the central role his ideas play in the philosophy of paleontology also reflects his articulation of some of the philosophic implications of his work, as well as the fact that he was reliably controversial.
But Steve was not the only important paleontologist active from the 1970s into the early 2000s, and from the standpoint of intellectual contributions to the discipline it is not clear that he was even the most important (a statement that I am sure will shock the continuing legions of FoGs – Friends of Gould). So here I want to broaden the view by identifying some major threads of recent paleontological work that raise issues that may be of interest to philosophers and where paleontologists might benefit from the philosophical attention. These are largely areas where Gould either wasn’t interested or only made tangential contributions. In a sense my foil here is Derek Turner’s Paleontology: A Philosophical Introduction (2011). I have no quarrel with Derek’s book, and indeed I am very glad that he wrote it, but most of the topics he addressed were those central to Gould’s work. So this post is by way of extending the scope of Derek’s book. In his first chapter, Derek distinguished between organismal and evolutionary paleontology, and like his book, I will focus here on evolutionary aspects of paleontology.
Preservation and the quality of the fossil record
What sorts of questions can paleontologists ask and expect to get reliable answers? As an undergraduate at Colgate in the late 1970s we did lots of paleoecology and the pages of Lethaia and other journals were full of “r and K selection in the Onondaga Limestone” (actually, I made that one up, but you get the point). At the time paleontologists thought a bed of fossils represented organisms all living and interacting at one time, so ecological approaches could be applied just as though the fossils were a living sample. All of this came to an abrupt end between 1980 and 1982 with papers on the resolution of the sedimentary record by Pete Sadler (Sadler 1981) at the University of California, Riverside, and, via a different approach, by David Schindel (Schindel 1980; 1982), then at Yale. These studies examined the nature of the sedimentary and fossil records and showed that in most cases, marine sediments could not be resolved to the level of ecological time. Thus, most paleoecological studies of the 1970s had been attempting to investigate ecological processes over thicknesses of rock that covered much longer intervals of time. But the impact of these papers spread far beyond paleoecology. A rich tradition of studies in taphonomy, sedimentary architecture and evolutionary paleoecology, along with greatly improved statistical methods have significantly improved our understanding of the quality of the fossil record, what questions we can reasonably ask, and which are interesting but difficult or impossible to answer. Paleontology is not yet up to the standards of research design in other fields such as biology, but things have improved greatly.
The realization that most assemblages included remains of animals that had lived at very different times, and in very different environments (known as time-averaging) turned out to be both a limitation and an opportunity. At a 1998 conference of paleontologists and ecologists we discovered that ecologists often binned their samples into longer intervals, artificially time-averaging them (essentially replicating what the fossil record provided to paleontologists), to avoid much of the noise that might obscure the signal under study. Time-averaging may ruin the ability to ask fine scale ecological questions, but it turns out to be a great opportunity for understanding longer-term macroecological processes. As ecologists turned from the study of meter-square quadrats to broader issues, ecologists and paleoecologists increasingly found themselves asking similar questions. The evolutionary paleoecology of today is much different than during the 1970s, but arguable much richer, focusing on larger-scale questions best addressed with fossil data rather than rather inanely copying papers published several years earlier in Ecology (as often seemed true in the 1970s). (Don Brinkman recently described this for vertebrate paleoentology).
The nature of biological diversity
As a graduate student at Harvard Jack Sepkoski began compiling a database of fossil occurrences, initially the first and last occurrences of families preserved in marine rocks, but eventually expanding to first and last occurrences of marine genera. Jack’s studies heavily influenced subsequent generations of paleontologists by providing a quantitative analysis of the waxing and waning of different clades of marine animals, characterizing mass extinctions, possibly with a periodic pattern, describing onshore to offshore shifts, and, I think somewhat unintentionally, leading to the idea one could do paleontology without doing field work. (I remained baffled as to why one wouldn’t want to do field work, but I digress…) Studies of diversity became an important focus of palebiology through the 1980s and 1990s, eventually morphing into the Paleobiology Database Project. There have been with continuing disputes about how best to measure diversity through time. But this raises a number of issues which I do not think have been well explored: Counting taxa is (relatively) easy to do, but is this the best way to assess the history of biodiversity? There are many other aspects of biodiversity, including biogeography (reasonably well studied), morphological disparity (ditto), to functional, developmental or phylogenetic diversity (little studied) or the structure of ecosystems. Aside from the long debates about how best to process PBDB data (in which I have lost what little interest I once had), what does global diversity even mean? It might be meaningful during intervals when global processes play a significant role in biodiversity, but regional mechanisms may control diversity much of the time. Gould’s focus on contingency, and the excitement over mass extinctions through the 1980s and 1990s may have led us to miss many other important aspects of biodiversity in macroevolution
Integrative studies of episodes in the history of life
Several decades ago the history of life on Earth was largely the purview of paleontologists: fossils were the main line of evidence and paleontologists interpreted fossils. Today many other lines of evidence have implications for the history of life on Earth and paleontologists have lost their privileged position. The discovery of evidence of extra-terrestrial impact seemingly associated with the end-Cretaceous mass extinction attracted the attention of other geologists, biologists and rafts of physicists. Molecular clock studies, molecular phylogenetics, comparative developmental biology as well as other geological disciplines have made vital contributions to understanding the early history of animals and the Ediacaran-Cambrian radiation. These and other episodes raise questions about how one weights the insights from different fields, varying standards of evidence, and what constitutes an explanation. How will paleontologists negotiate their interactions with other approaches to evolution in deep time, such as molecular clock studies, phylogenetic comparative methods or geobiology?
Macroevolution and Novelty
True, much of Gould’s work focused on macroevolution and that is the focus of his final work Structure of Evolutionary Theory. But developments since his death have taken macroevolution in new directions, and raised important questions. Comparative evolutionary developmental biology (“evo-devo”) began in the late 1990s with the utterly unexpected discovery of highly conserved developmental genes, and later gene networks. Accompanying the work on evo-devo has been a resurgence of interest in the nature and mechanisms behind evolutionary novelty. Punctuated equilibria, species selection and even the evolutionary impacts of mass extinctions are, to use Peter Godfrey-Smith’s terms, distributional accounts of evolution. But evo-devo has returned the focus to whether there are also distinctive origin accounts of macroevolutionary patterns. Several philosophers of biology, particularly Alan Love and Ingo Brigandt, have been very interested in the nature of novelty but from a more biological perspective. But the fossil record raises other questions: is novelty a distinctive form of macroevolution? Is there more than one kind of novelty? Do novelties respond to existing opportunities or do organisms construct their own opportunities via niche construction? Much of macroevolutionary theory seems to view the Ediacaran-Cambrian explosion of animals as a unique event in the history of life, somehow different from the macroevolutionary processes operating from the late Cambrian to today. Was it really unique (and why?), or do we need to reformulate approaches to macroevolution? Finally, how do issues of macroevolution fit with calls for an ‘extended evolutionary synthesis’?
The nature of paleontology and paleobiology as scientific disciplines
The development of disciplines is of interest to both philosophers and historians of science, and paleontology provides an interesting case study because it has been at the intersection of geology and biology since the 19th Century, drawing techniques and questions from each. David Sepkoski’s outstanding history of the growth of paleobiology as a field, Rereading the Fossil Record (2012), illustrates some of the possibilities. Fossil material is embedded in a geological context, but in studying fossils we often pursue biological questions. To what extent does paleontology have unique questions which would not be posed by other geologists or biologists? What does this mean for the future of paleontology and paleobiology as disciplines?
I could go on, and I haven’t even touched equally interesting philosophical problems associated with organism-centered aspects of paleontology. I have spent many years involved with the Santa Fe Institute, a private research foundation that focuses on complex adaptive systems. There are lots of physicists involved with SFI, and I have been fond of pointing out to some of them that if they were really as smart as they think they are they would study something hard. Like paleontology. (Yes, it is true – I enjoy annoying physicists. Everyone needs a hobby.) How hard can physics really be? A limited number of subatomic particles which have basically been doing the same things for 13+ billion years. Paleontology takes the complexities of biology through the 3.8 (or 4.2, or 4.4) billion years of life on Earth. Surely the philosophical problems of the history of life deserve some fraction of the efforts expended on physics? Time to look beyond the headlines, and beyond Gould, to address the many other interesting questions.
Douglas Erwin is a Senior Scientist and Curator of Paleobiology at the National Museum of Natural History (part of the Smithsonian Institution). His current projects focus on the nature of evolutionary novelty and innovation through the history of life, but with particular interest in the Ediacaran-Cambrian early history of animals. In 2013 he and Jim Valentine published The Cambrian Explosion (Roberts). Previous work has involved the causes and time of the end-Permian mass extinction and the evolution of gene regulatory networks.
Thanks to Adrian Currie for inviting this, and for comments on an earlier draft.
Sadler PM. 1981. Sediment Accumulation Rates and the Completeness of Stratigraphic Sections. Journal of Geology 89(5):569-584.
Schindel DE. 1980. Microstratigraphic sampling and the limits of paleontological resolution. Paleobiology 6:408-426.
Schindel DE. 1982. Resolution analysis: a new approach to the gaps in the fossil record. Paleobiology 8:340-352.