This is a rather different entry than my usual posts on this blog. A few months ago, Brian Beatty and I published Jeffersoniana 20, in which we presented some ideas on feeding behaviors and lateralization in fossil whales. We received generally positive feedback, but also some mild criticism for engaging in such speculation. I began to wonder, had we gone too far? What, in fact, is “too far”, and what role does speculation have in paleontology?
There would certainly seem to be a sliding scale to consider here. I think that practically everyone would agree that speculation that dinosaurs were alien visitors from another planet is not worthy of consideration. But what about speculation that Tyrannosaurus was an obligate scavenger?
Context is also important. It would be ridiculous to speculate that fossils were all deposited in a single global flooding event. But 200 years ago, presenting such an idea would not have been outrageous. Likewise, 50 years ago it was reasonable to suppose that Brachiosaurus had nostrils on the top of its head as an adaptation for living under water (and its large size and small teeth were used as supporting data). Were workers at that time wrong to engage in their speculations, even though they have since been shown to be incorrect?
The example of Tyrannosaurus is illustrative. The genus has been known for more than century, and for the first 75 years after its discovery it was generally assumed to be a predator (with varying levels of “activity”). Yet in the 1990’s Jack Horner in particular began to argue that Tyrannosaurus was a pure scavenger. This was not just an idle claim, but was based on particular observations about tyrannosaur anatomy.
Was Horner right? I think most current paleontologists would say, only partially at most. But the flood of research that has resulted from Horner’s speculation has been impressive. There have been seemingly endless studies coming at the scavenging/predator issue from completely novel angles: leg proportions and cross-sectional strength, tooth strength, brain anatomy, injuries and physical capabilities of potential prey animals, ecology of modern scavengers and predators. So, maybe Horner was wrong (or only partially correct) in his speculations, but how much more have we learned as a result?
Paleontology is replete with such examples. The impressive bioengineering studies on sauropods were initially done to test the idea of aquatic sauropods. At least three different groups have been suggested in succession as whale ancestors (creodonts, mesonychids, raoellids); when each was proposed it seemed like an excellent idea at the time, and each proposal resulted in a massive amount of research to test it. Even the idea of a causal relationship between bolide impacts and mass extinctions started as an attempt to explain a single anomalous datum, an elevated amount of iridium in rocks at the end of the Cretaceous. Thousands of scientific papers have been published as a result.
When I was a graduate student, I had to present my proposed research project to my committee. One member commented that he wasn’t sure I was looking at enough specimens to reach any definite conclusions. In response, I pointed out that I was already looking at every known specimen of this group that had ever been found in North America. What more could I do, short of ignoring the group altogether?
Paleontology lives on the edge of science. In saying this I don’t mean to imply that paleontology is less scientific than, say physics or chemistry. Rather, we work in a field in which data is almost always limited. We go out on a limb a lot, and we’re sometimes wrong as a result. Almost every talk at a paleontology meeting ends with a slide that lays out what the next research steps will be, and almost always that slide includes words to the effect that “we need more specimens”.
These principles apply whether the research is as grandiose and far-reaching as the cause of mass extinctions, or as modest and focused as the feeding habits of an obscure species of baleen whale. Brian and I may or may not have been correct in every suggestion that we made (although I feel good about all of them). But if the paper results in someone developing a new technique to look at whale dietary preferences, or looking more closely at pathologies, or considering postcranial anatomy in their studies, or looking at the evolution of baleen more critically, it will have been a success.
It’s great to be right about an idea, but I’m always a little suspicious when someone is certain they’re right. I’ve been wrong enough to be uncertain about my (and other’s) conclusions. But the fact that you might be wrong shouldn’t paralyze you into inactivity. If you propose a reasonable idea and someone else comes up with a new way to look at the problem that shows you were incorrect, you have still contributed to the field. Because of the fallout of your idea, we know more than we did before. Paleontology thrives on such speculation.
Speculation is important, because you never know where it will lead…