* This is Part 2 of a two-part essay on speculation in geohistory. In Part 1 I introduced the problem and discussed three examples of outrageous speculation (the Triassic kraken, Nemesis, and vendobiont hypotheses, respectively). Part 2 aims to make sense of their reception by developing and then using the concepts of “well-controlled” and “dangerous speculation.” This requires a quick review of the literature on speculation in the historical sciences, which is where I begin. “Problematica” is written by Max Dresow…

Philosophers on speculation

The literature on speculation in the historical sciences is mostly a response to the account put forward in Currie (2018). According to this account, historical scientists are warranted in practicing “empirically-grounded speculation” whenever they find themselves in “unlucky” epistemic circumstances. Circumstances count as “unlucky” when direct (trace) evidence is scarce or highly decayed, rendering hypotheses about the past massively underdetermined. Speculation is “empirically grounded” when it outruns the empirical evidence and “generates epistemic or empirical goods that increase epistemic traction” (Currie 2018, 289). So, Currie’s argument is that speculation that outruns the evidence can scaffold inquiry in situations of evidential scarcity, guiding the search for evidence and facilitating the development of new techniques and approaches that might not otherwise be developed. And the unluckier the circumstances, the longer the leash for speculative adventures: “Especially when the going gets tough… historical science should be wild, messy and creative” (Currie 2018, 291).

AI generated image of a “philosopher of paleontology at work” (via OpenArt)

The first thing to say about this account is that it is normative. Its aim is to recommend speculation as an appropriate response to certain epistemic situations, which Currie takes to be typical of the historical sciences: “[in] historical investigation… empirically grounded speculation is the way forward” (Currie 2018, 290, emphasis added). Apropos of this aim, Currie is more concerned with the benefits speculation can provide than with its drawbacks and pitfalls. However, as Derek Turner (2019) has argued, the drawbacks of speculation require scrutiny as well. Two shortcomings, in particular, work against the epistemic benefits highlighted by Currie. The first involves failures of reflexivity: some speculations manifestly fail “to scramble existing assumptions or nudge us out of our cognitive ruts” (Turner 2019, 4). The second involves misinformation. Some speculation conveys a positively misleading impression of the subject matter, by ignoring relevant facts or presenting them in a misleading way. Responding to Turner, Currie (2019) lumps together failures of reflexivity and fidelity-to-data as “egregious speculation.” This term refers to speculation that not only fails to advance research, but actively undermines it. In contrast, “idle speculation” fails to advance research towards an epistemic goal without actively undermining it. (Consider an otherwise inoffensive hypothesis that provides no pointers for investigation, if such a hypothesis can be imagined.)

Putting all this together, we can generate a threefold taxonomy of speculation:

“Empirically grounded” or productive speculation: speculation that helps a community reach its epistemic goals by opening new routes of empirical knowledge
Idle speculation: speculation that neither promotes nor thwarts a community in reaching its epistemic goals
Egregious speculation: speculation that actively thwarts a community in reaching its epistemic goals

Notably, this taxonomy traffics in results, and is therefore mute about what makes speculations productive, idle, or egregious in the first place. However, Turner’s remarks indicate that we are not entirely in the dark here. A hypothesis that misrepresents the facts is unlikely to be a productive one. Likewise a hypothesis that reinforces an existing idea that lacks evidential support. To investigate the reception of speculative hypotheses, we need more constraints like these: constraints that illuminate why some speculative hypotheses are taken to be epistemically acceptable while others are treated with suspicion or disdain (Turner 2019, 4).

This is what the ideal of well-controlled speculation aims to provide. Specifically, it aims to provide a set of constraints corresponding to (what are often taken to be) minimal requirements on successful scientific hypotheses. Well-controlled speculation does not provide a standard for judging speculations as productive or unproductive (although extremely uncontrolled forms of speculation are unlikely to yield true claims about the world). Instead, it provides a framework for analyzing bits of speculation in relation to the putative good- and bad-making qualities of hypotheses in general. It will be useful to the extent that it helps us distinguish different kinds of risky speculation, including speculation that fails to measure up to the ideal while nonetheless meriting a favorable reception in a scientific community.

Well-controlled speculation can be characterized in terms of four constraints or requirements. The first is fidelity-to-data: speculation should not omit relevant facts or otherwise misrepresent the data it appeals to. The second is reflexivity: speculation should not reinforce ideas lacking evidential support or other biases that lead to faulty inferences. The third is coherence: speculation should cohere with robustly established results in areas germane to the speculation (if a hypothesis fails to agree with the best knowledge in an area, then that is usually points against it). And the fourth is parsimony: speculation should not multiply entities beyond necessity, or frame more complicated accounts when simpler ones fulfill the relevant adequacy criteria. Of these, the first and second constraints cannot be relaxed without harm. To relax either the fidelity-to-data or reflexivity requirements is to engage in egregious, or at the very least idle, speculation (Turner 2019; Currie 2019). The third and fourth constraints, by contrast, are relaxable under certain circumstances. Relaxing either or both leads to what I call “dangerous speculation.” This is speculation that, while it need not be egregious or idle, is perhaps more likely to represent a false start or dead-end than more well-controlled speculation. Put differently, dangerous speculation is a risky epistemic game.

It is clear that dangerous speculation is warranted under certain circumstances. As Davis observed in 1926, many advances in the history of geology were “made by outraging in one way or another a body of preconceived opinions” (464), and this was before the acceptance of continental drift furnished the best example in the history of science of dangerous speculation vindicated (Oreskes 1999). But issues of warrant are not my interest here. Instead, I am concerned with those factors that influence the reception of dangerous hypotheses, and whether any of them contain epistemic lessons. To get a handle on this, I turn in the rest of this essay to an analysis of the cases discussed in Part 1.

Dangerous Speculation in the Balance

Kinds of Dangerous Speculation

This essay has discussed three examples of outrageous (I would now say “dangerous”) speculation. These met with very different receptions. The Triassic kraken hypothesis was dismissed with either a huff or a snicker, depending on the person. The Nemesis hypothesis garnered a more mixed response. Many paleontologists were skeptical or even dismissive, but others were responsive, and astronomers seem to have been positively enthusiastic about it. Finally, Seilacher’s vendobiont hypothesis was for the most part well received, even though cogent criticisms prevented its widespread acceptance in its original form. What are we to make of this pattern?

Diorama of the Ediacaran Biota from the Field Museum in Chicago

The first thing to say is that the pattern has a clear non-epistemic texture. Raup was a member of the National Academy of Sciences when he speculated about extinction periodicity, and Sepkoski was fast becoming the most influential paleontologist of his generation. Seilacher too was a scientific star: in Gould’s estimate, “the finest paleontological observer now active” (Gould 1989, 312). This charged their speculations with a credibility that McMenamin could not access, and in Raup and Sepkoski’s case, enabled them to publish in the widely-read (and lightly edited) journal PNAS, much to the consternation of their colleagues. However, McMenamin was far from a nobody in 2011. His work on the Ediacaran biota was widely known and well cited (e.g., McMenamin 1986), and when Seilacher was awarded the prestigious Paleontological Society Medal in 1994, it was McMenamin who presented him the award. This indicates that McMenamin occupied a non-marginal standing in the paleontological community, at least before he released the kraken at the 2011 GSA. Still, the disparity between his reputation and those of Raup, Sepkoski and Seilacher was considerable, as Prothero’s remarks indicate (see Section 1).

There is no reason to shrink from the implication. Were it possible to perform a factor analysis on the results I have presented, the first factor would correspond to a non-epistemic influence, and would probably explain a fair amount of the data. I grant this and am interested in exploring whether any of the remaining factors have epistemic dimensions. It is my contention that they do, but to appreciate this it will first be useful to introduce a few additional terms corresponding to kinds of dangerous speculation.

Dangerous speculation is speculation that relaxes one or more constraints on well-controlled speculation. Given this understanding, it is possible to distinguish three types of dangerous speculation based on the constraint(s) relaxed. Speculation that relaxes the coherence constraint while maintaining fidelity-to-data, reflexivity, and parsimony may be termed “revisionary speculation.” Speculation that relaxes parsimony while maintaining fidelity-to-data, reflexivity, and coherence can be termed “extravagant speculation.” Finally, speculation that relaxes both coherence and parsimony while maintaining fidelity-to-data and reflexivity can be termed “wild speculation.” These terms are summarized in Table 1. Notice that the types of dangerous speculation are distinct from the types of egregious speculation discussed by Turner (2019) and Currie (2019), which involve relaxing either the fidelity-to-data or the reflexivity requirements.

Table 1. The four constraints associated with well-controlled speculation, and the kind of speculation that results when one or more of them are relaxed. (Observed constraints are marked with a ‘+’, unobserved constraints with a ‘–’.) Note that revisionary, extravagant, and wild speculation are all instances of what I call “dangerous speculation.”

I regard the Nemesis hypothesis as an example of extravagant speculation shading into wild speculation. The reason is that, while its assault on parsimony was severe (making it extravagant), it also represented a challenge to existing beliefs about extinction whose impact was blunted, without being removed, by debates surrounding the Alvarez hypothesis. It follows that in considering the reception of Nemesis, we must keep track of both its challenge to coherence (owing to the postulate of extinction periodicity) and its flouting of parsimony (in the form of two hypothetical objects: Nemesis and the Oort cloud). The latter feature makes it an extravagant hypothesis par excellence, especially considering that the only evidence for the existence of Nemesis was contained in the extinction data.

The vendobiont hypothesis, by contrast, is an instance of revisionary speculation. It involves no general loosening of the parsimony requirement.* Indeed, what was outrageous about Seilacher’s suggestion was just how parsimonious it was: how it managed to render nearly all the characteristic Ediacaran forms as variations on a single shared body plan. However, from a coherence standpoint, the hypothesis was scandalous, casting aside nearly the entire framework of interpretation developed by Glaessner and his associates. Arguably it was this radical challenge to the traditional framework that stimulated the burst of interest in the Ediacaran biota that began in the 1990s and continues unabated to the present day.

[* I say “general” here because one aspect of Seilacher’s hypothesis was not so parsimonious. This was the postulate of a cuticle with “rather incompatible properties: flexible, but able to become creased and fractured; watertight…yet permeable enough to metabolically interact with the environment; cuticular, but expandable during growth” (Seilacher 1989, 237). Gehling’s “death mask” hypothesis was an attempt to save the same phenomena without postulating such an improbable structure.]

What about the kraken? To begin, it is deeply unparsimonious, both because it postulates the existence of a “kraken” on the strength of no evidence besides that which it purports to explain, and because nothing in the evidence seems to demand so exotic an explanation. But it is also seemingly at variance with existing knowledge of cephalopod evolution, since the limited fossil record suggests that a Triassic coeloid would have just one row of suckers, as opposed to the two required by the postulate of self-portraiture (Greenfield 2021). A giant cephalopod would also have massively exceeded its contemporaries in size (no Triassic forms are thought to have exceeded one meter in length) and, at 30 meters, would represent a >90% increase over the next largest member of the taxon (including all known members, past and present). In short, hypotheses don’t get much wilder than this, notwithstanding that none of the above reasoning invalidates the hypothesis in the strictest sense.

The kraken is an extreme case of wild speculation, and functions here mainly as an outgroup comparison for more acceptable forms of speculation. What it illustrates is that there are limits to the “wild, messy and creative” postulates that historical scientists will put up with, even under conditions of evidential scarcity. (There is such a thing as “too wild,” pace Davis’s claims about outrageous hypotheses and Currie’s reasonable optimism about speculative hypotheses.) To be clear, the problem is not that the Triassic kraken hypothesis furnishes no scaffolds for inquiry. Before McMenamin came along, no one dreamed of looking for evidence of giant cephalopods in the Nevada desert. It is rather that the scaffolds it provides are so rickety that no one wants to mount them. Speculation this wild is unlikely to be productive speculation.

An ichthyosaur, the kraken’s supposed victim. Art by R. J. Palmer

But how different is this from Nemesis? After all, the Nemesis hypothesis implicates two hypothetical objects related to each other in a very specific way, and all this to produce a disputed effect (extinction periodicity). By contrast, the kraken hypothesis manages with one hypothetical object to produce its disputed effect (a midden/portrait). Yes, there are independent reasons for thinking that a giant coeloid equipped with biserial suckers is implausible. But there were independent reasons for disbelieving in Nemesis as well, chief among them worries about the stability of its orbit over so long a period. In addition, the Nemesis hypothesis constituted a challenge to prevailing beliefs about extinction, mostly owing to its endorsement of extinction periodicity. This is why I called it an instance of extravagant speculation shading into wild speculation.

Here, three remarks are in order. The first is that the Nemesis hypothesis, while it sought to explain a disputed phenomenon, was nonetheless based on an analysis of the most extensive dataset that had ever been compiled for the purposes of analyzing trends in marine diversity over time. This alone lent it some credibility, even if it did not remove all worries about the quality of the data (recall Hoffman’s criticisms about the importance of arbitrary decisions concerning the dates of stratigraphic boundaries). The second is that Raup and Sepkoski’s analysis of extinction periodicity, for all its uncertainty, was highly suggestive—even tantalizing. Everyone agreed that if claims of periodicity could be solidified, then the phenomenon would require a special explanation, and probably an extraterrestrial one. This is because the pattern was unlikely to have arisen by chance and no one could think of an earthbound process that operated periodically over so long an interval. The contrast with the kraken here is sharp, since the Berlin Ichthyosaur Death Assemblage strikes most observers as just another bonebed, and hardly the sort of thing that requires a special explanation.

Third, claims of extinction periodicity (and by extension, hypotheses marshaled to explain them) were part of a developing research program that had gained serious momentum by 1984. This was the research program variously called “evolutionary” or “nomothetic paleobiology,” and that included Sepkoski’s early work on Phanerozoic marine diversity trends, as well as Raup’s work on extinction and clade dynamics (Sepkoski 2012). It also included Stephen Jay Gould’s work with Raup and Sepkoski, which probably accounts for Gould’s enthusiasm for Nemesis (Shiva). As Gould saw it— and others doubtless agreed— discussions of periodic extinction were a good thing for paleontology. They highlighted the utility of a particular way of working, which leveraged the power of computers to analyze large-scale patterns in the history of life. And they illustrated the potential of paleontology to contribute new insights about the workings of evolution over geological timescales. In Gould’s words, “The cyclical theory of catastrophic extinction leaves paleontologists in the driver’s seat with a decade of exciting work in front of us” (Gould 1985, 446). Here is yet another contrast with the kraken. Unlike McMenamin’s hypothesis, Raup and Sepkoski’s work was part of an emerging project that Lakatos might have called a “progressive research programme.” This gave it both an audience and a claim to relevance that the kraken could not muster.

Turning to the vendobiont hypothesis, things were different. While Seilacher was the leader of a thriving group of paleontologists at Tübingen, his constructional analysis of the Ediacaran biota was too idiosyncratic to assimilate to any tradition in Precambrian paleontology. This left Seilacher as a lone voice in the wilderness— or at least as close to a lone voice in the wilderness as the most famous paleontologist in Germany could be. The contrast with Raup and Sepkoski was sharp. Yet the vendobiont hypothesis had several things going for it, including things the Nemesis hypothesis arguably did not. Perhaps the most important was that, in disrupting nearly every feature of the received interpretation, it cleared space for a renewed look at the affinities, taphonomy, and paleoecology of Ediacaran organisms, just as the resources were becoming available to push these investigations forward. In the years following Seilacher (1989), nearly every aspect of Ediacaran paleobiology came in for renewed interest and scrutiny. No better evidence exists than Gehling’s (1990) article, which uses Seilacher’s proposal to motivate a far-reaching reassessment of the life, death and classification of Ediacaran organisms. Nemesis, by contrast, set a narrow research agenda mostly focused on locating the Nemesis object itself— a task for which paleontologists were singularly ill-equipped.

Two Epistemic Lessons

I suspect that the potential for stimulating open-ended research is a general feature of revisionary speculation (speculation that relaxes the coherence restraint). At least when it is successful, such speculation will be capable of stimulating diverse lines of research aimed at reconciling old observations with new frameworks, resolving ambiguities, and tidying up conceptual and taxonomic categories. Even if a speculative hypothesis is ultimately rejected, it may stimulate a significant amount of research while it remains under discussion, especially if it is sufficiently compelling to undermine confidence in prevailing categories and approaches. This is basically what happened with the vendobiont hypothesis. Few paleontologists accepted it whole hog, but fewer still dismissed it as obviously wrong or unmotivated. This created the conditions for a “free-for-all” in Ediacaran paleontology, with important consequences for ongoing research on these enigmatic organisms (Narbonne 2005, 431).

From this we can extract a provisional epistemic lesson: that the tolerance a scientific community exhibits for revisionary speculation depends, in part, on how fruitful a hypothesis is in stimulating diverse lines of open-ended research. Even outrageous hypotheses like Seilacher’s may find a relatively warm reception if they suggest diverse research questions, as the vendobiont hypothesis manifestly did. By contrast, a hypothesis that fails to suggest new questions— or that suggests only a few questions of narrow scope— is likely to get the brush-off (Currie 2021). The Triassic kraken hypothesis has many problems, but one of them is that it doesn’t open up new lines of research apart from a needle-in-the-haystack search for the remains of a giant cephalopod. Had the kraken been shown to exist from independent evidence, then a range of questions would have arisen about its morphology, phylogenetic affinities, and ecological relationships. But in the absence of such evidence, these questions remain in the realm of cryptozoology as opposed to professional paleontology. Simply put, there isn’t much you can do with a giant kraken (and ditto, to a lesser extent, a killer star).

Recent work on the anatomy of *Charnia masonia—* a vendobiont by Seilacher’s lights, and in some ways a testament to the enduring influence of his ideas: “Our data reveal a highly compartmentalized internal anatomy for Charnia, reminiscent of the quilted pneu structure inferred by Seilacher for what he perceived to be a clade of Vendozoa” (from Dunn et al. 2021)

So communities may be willing to relax coherence requirements when revisionary speculation suggests diverse lines of open-ended research. Does the same thing hold for parsimony requirements and extravagant speculation? Perhaps. But in the case of the Nemesis hypothesis (my main example of extravagant speculation), something else was going on. To the extent that paleontologists were amenable to Nemesis, it was because the hypothesis sought to explain a potentially important phenomenon known from copious and apparently reliable empirical evidence. Of course, extinction periodicity was unconfirmed, and this cast a pall of suspicion over the entire affair. But few would have denied that extinction periodicity was an important finding if true, and this created a demand for explanation even in the absence of a knock-down demonstration of periodicity. It was the recognition of this demand, paired with the absence of a workable explanation based on known factors, that prompted some to entertain the possibility that otherwise unknown objects might participate in the relevant causal mechanism.

Generalizing again, we may hazard that the tolerance a scientific community exhibits for extravagant speculation depends, in part, on whether there exists an independently characterized phenomenon that generates formidable demands on explanation and that strikes community members as requiring an explanation. Where such demands exist (and especially where the rewards for successful explanation are high), extravagant speculation is likely to be tolerated. Where they are absent, speculation is likely to be ignored or criticized. Again, the kraken provides a useful comparison. Here, there was no independently characterized phenomenon that was widely seen as imposing formidable demands on explanation. An honest-to-goodness midden composed of ichthyosaur skeletons might have fit this bill, but McMenamin failed to convince anyone that such an interpretation ought to be entertained. The contrast with claims of extinction periodicity is sharp. Periodicity raised many eyebrows, but nonetheless found its way into the pages of Nature. To my knowledge, no one has discussed the Triassic kraken hypothesis in a scientific publication apart from McMenamin himself: a conspiracy of silence reflecting a lack of confidence that the bonebed can be characterized as a midden.

Let's Speculate!

I began this essay by asking what accounts for the relatively warm reception of the vendobiont hypothesis, the mixed reception of Nemesis, and the heckling dismissal of the Triassic kraken. Part of my answer has been to suggest that these hypotheses, while all “dangerous,” stretch credulity in different ways. The vendobiont hypothesis is an example of revisionary speculation; Nemesis represents extravagant speculation shading into wild speculation; and the kraken is almost indecently wild. This helps to account for the brusque dismissal of the Triassic kraken, since wild speculation flies in the face of multiple norms of responsible inference. But it fails to differentiate Nemesis and the Vendobionta, since there is little in these norms that favor extravagant speculation over revisionary speculation or vice versa. Here, I suggest that thinking in terms of tradeoffs may be helpful. Scientific communities will relax coherence requirements on speculative hypotheses to the extent that a hypothesis is fruitful in generating new lines of research. The vendobiont hypothesis is fruitful in exactly this way; hence it received a relatively warm reception, despite the difficulties that were evident to expert critics. I have also suggested that communities will relax parsimony requirements to the extent that a hypothesis addresses the demands generated by an independently characterized phenomenon. This accounts for the positive aspects of Nemesis’s reception. But claims of periodicity had yet to be vetted when Nemesis was proposed, and many paleontologists found them hard to believe. Some were thus unwilling to entertain this bit of extravagant speculation, at least until the 26-million-year extinction cycle had been independently validated.

Rightly understood, these are modest claims. I am not saying that communities only tolerate revisionary speculation when it opens up diverse avenues of open-ended research. Nor am I saying that communities only tolerate extravagant speculation when it addresses the demands generated by an independently characterized phenomenon. Rather, I am arguing that weaker associations obtain between these variables, which nonetheless help us make sense of the reception of dangerous speculation in geohistory and beyond.

Regardless of whether this analysis is successful, I submit that it is useful to characterize different forms of dangerous speculation as loci for philosophical engagement. This allows us to pose new questions, like how much do communities differ in their tolerance for extravagant speculation, and (how) does this relate to features of their epistemic situations? We can also ask whether there are situations in which dangerous (extravagant, revisionary) speculation is likely to be epistemically productive as opposed to idle or deleterious. Too often, philosophical accounts of speculation have been content to explain the benefits of speculative practices while ignoring their drawbacks. This is because most accounts of speculation have taken as their foil the notion that speculation is an irresponsible policy. But to achieve a richer picture of scientific speculation, philosophers must weigh benefits against drawbacks in a more explicit way. The project is likely to be a difficult one, but is no less important for this. Perhaps it even calls for some philosophical speculation: empirically-grounded, but not opposed to a bit of danger.

References

Currie, A. M. 2018. Rock, Bone and Ruin: An Optimist’s Guide to the Historical Sciences. Cambridge (MA): The MIT Press.

Currie, A. M. 2019. Epistemic optimism, speculation and the historical sciences. Philosophy, Theory and Practice in Biology 11. https://doi.org/10.3998/ptpbio.16039257.0011.007.

Currie, A.M. 2021. Science & speculation. Erkenntis https://doi.org/10.1007/s10670-020-00370-w.

Davis, W. M. 1926. The value of outrageous geological hypotheses. Science 1636:463–8.

Gehling, J. G. 1990. The case for Ediacaran fossil roots to the metazoan tree. In B.P. Radhakrishna (ed.), The World of Martin Glaessner, 181–224. Bangalore: Geological Society of India.

Gould, S. J. 1989. Wonderful Life: The Burgess Shale and the Meaning of History. New York: W.W. Norton & Co.

McMenamin, M. A. S. 1986. The garden of Ediacara. Palaios 1:178–82.

Oreskes, N. 1999. The Rejection of Continental Drift: Theory and Method in American Earth Science. Oxford: Oxford University Press.

Seilacher, A. 1989. Vendozoa: organismic construction in the Proterozoic biosphere. Lethaia 22:229–239.

Sepkoski, D. 2012. Rereading the Fossil Record: The Growth of Paleobiology as an Evolutionary Discipline. Chicago: University of Chicago Press.

Turner, D. 2019. Speculation in the historical sciences. Philosophy, Theory and Practice in Biology 11. https://doi.org/10.3998/ptpbio.16039257.0011.011.