Following up on the post in which I examined how the SVP Ethics Education Committee responded to the allegations of unethical conduct that have come to be known as "Aetogate," this post will discuss what the committee identifies as the "lessons learned" from this investigation. Once again, I'll be drawing from the Statement from the Executive Committee (PDF). The third post will consider the "best practices" (PDF) proposed by the committee.
The Statement from the Executive Committee enumerates seven "lessons learned," couching these in terms of ways "these conflict might have been avoided." I'll take each of them in turn.
1. Don't eat your young.
First, science is both an individual and a social process. Achievement involves not only individual and collaborative discoveries and publications, but also support of other workers, especially junior scientists, in one's scientific community. Overly competitive behavior does not necessarily further our discipline.
Let's underline this point. Certain types of behavior by senior members of a professional community may have the effect of killing off the community's young. Not just the "weaklings" who needed to be thinned from the herd, either -- potentially a whole generation of workers in the field can be harmed by a community that does not treat those junior members as legitimate members of the community whose interests ought to be protected. (We've seen some evidence of that kind of attitude around this case.)
Junior people in vertebrate paleontology seem almost guaranteed to be at a disadvantage in competitions with senior members, at least in terms of funding, access to collections, and the network of professional peers on whose help they can call. In a no-holds-barred competition, it's not a fair fight.
To the extent that the discipline's future health -- and its very existence -- depends on the training of new generations of scientists and the integration of these scientists into the activities of the community, they need to be nurtured. Collaboration with and support of other workers need to be nurtured.
One would hope this means that there are something like tangible career rewards for collaboration with and support of other workers, rather than just for crossing the finish line first.*
2. Who's responsible for dealing with bad behavior by members of the professional community?
[W]hile neither the allegations of Martz at al. nor those of Parker are explicitly covered under the SVP Ethics Bylaw, the allegations do concern matters of professional conduct and propriety. Matters such as plagiarism and theft lie partly in the domain of SVP as a scientific society, but they are more directly the responsibility of employers and journal editors as well as individuals. We expect reviews of professional conduct to be unbiased an free of conflicts of interest (real or apparent), regardless of whether they are performed by professional societies, employers or editors.
Are those expectations of employers or editors always realized? It would appear not.
This "lesson" strikes me as somewhat ambiguous. If the point is that employers and journal editors ought also to be serious about ensuring good professional conduct on the part of their employees and authors, then it seems obviously true (at least to members of a professional community like paleontology, if not to university administrators and journal editors). But there seems also to be an acknowledgment here (in the wording of what is not "explicitly covered" by the bylaws but is nonetheless a matter of "professional conduct and propriety") that the spirit of the law, not just the letter of the law, matters.
If there's anything this case seems to show, it is that employers and journal editors may find a multitude of reasons not to take allegations of wrong-doing against their employees or authors seriously. Universities, museums, and journals all have many interests, some of which may lead them to minimize the legitimate interests of parties not in their employ (or editorial board). Moreover, ignoring or minimizing allegations promises to be less resource-intensive than mounting thoroughgoing investigations of those whose names and prestige are already linked with yours.
But was the alleged misconduct primarily a matter of offenses against an employer, or against a journal editor? Or is it more properly understood in terms of offenses against a professional community and its members?
There are lots of entities here that probably -- according to their own official rules -- ought to be involved in policing bad behavior when it happens. However, given that the kinds of bad behavior alleged are ultimately doing harm to the functioning of the paleontology community, that community needs to be actively involved in responding to it.
3. Conclusions in paleontology strive for reproducibility, too.
[S]pecialists working separately on the same fossil material can indeed independently reach the same conclusion about morphology, taxonomy, or other aspects of the fossils. Indeed the foundations of our science are based on the premise that repeatable conclusions can be reached objectively by independent study of the same material. Intellectual theft, therefore, can be difficult to prove without specific documentation that goes beyond, for example, similarities in anatomical description.
In theory, if paleontology is an enterprise directed at building a body of knowledge that is well-tested, it should be a good thing when independent specialists come to the same conclusions. Indeed, to the extent that the knowledge is the aim of the enterprise, paleontologists should want others in their field closely to scrutinize their own conclusions, to identify weakness and present challenges -- to make sure the conclusions end up being as firm as they can be without going beyond what the empirical evidence will support.
If the finish line is something like truth (or at least well-supported logically coherent conclusions), the expectation is that multiple paleontologists will arrive there -- maybe in close temporal proximity. But the reward structure is winner-take-all: only the first across the finish line gets credit.
This reward structure provides a strong incentive to commit intellectual theft in conditions where intellectual theft is hard to prove. Perhaps this is reason enough to consider whether this is the best reward structure from the point of view of the knowledge-building aims of the professional community.
4. Objectivity doesn't just happen.
[T]he editorial practices of the New Mexico Museum of Natural History and Science Bulletin have left the authors vulnerable to the appearance of impropriety. Authors, including volume editors, have commissioned reviews of their own manuscripts; manuscripts have been reviewed in-house by other Museum personnel; and journal editors have made decisions about whether to accept their own papers for publication. These procedures do little to protect authors from charges of inappropriate conduct, should such charges be made in error.
I might add, these procedures do little to protect authors from charges of inappropriate conduct in the case that such charges are fully warranted. (I hope the SVP Ethics Education Committee was not denying the possibility that such charges might be warranted.)
In any case, the judgment here is that editorial practices of the sort used by NMMNHS Bulletin are not sufficient to ensure stringent peer review. Such stringent peer review is needed to make the knowledge paleontologists are adding to the shared body of knowledge as objective as possible. So the community is better off with journals with stricter editorial practices.
5. Communication could head off problems like these ...
[L]ack of communication can exacerbate conflicts such as these two. For example, if Parker had notified Lucas and colleagues in 2006 of his accepted manuscript naming the new genus and sent them a copy of the manuscript, then it would have been clearly unethical for Lucas et al. to move forward with their own publication. Similarly, when Lucas et al. first became aware that Parker intended to publish upon the fossils that Lucas and colleagues were (to their minds, exclusively) studying, it would have been prudent for Lucas or his colleagues to contact Parker about the apparent conflict.
There are a lot of assumptions kicking around here about what would and would not be prudent, as well as about how the burdens of transmitting and receiving information ought to be distributed.
The first question is whether publications and abstracts count as "communication" within a scientific community. Lucas and colleagues claim "they were unaware of his [Parker's] intentions to publish a new name, noting that they knew only that Parker considered the genus assignment incorrect."
Parker asserted that "Desmatosuchus" chamaensis did not belong to the genus Desmatosuchus in the following:
- His 2003 thesis, in which he asserted the generic separation and assigned this species to a new genus, Heliocanthus.
- Three published papers (Parker, W. G. 2005. Faunal review of the Upper Triassic Chinle Formation of Arizona. Mesa Southwest Museum Bulletin 11:34-54; Parker, W. G., and R. B. Irmis. 2005. Advances in Late Triassic vertebrate paleontology based on new material from Petrified Forest National Park. New Mexico Museum of Natural History and Science Bulletin 2:45-58; Parker, W. G. 2006. The stratigraphic distribution of major fossil localities in Petrified Forest National Park. Museum of Northern Arizona Bulletin 62:46-61.).
- Two published abstracts in the Journal of Vertebrate Paleontology (Parker, W. G. 2003. Revised taxonomy of the Late Triassic aetosaur Desmatosuchus (Archosauria: Crurotarsi) from the southwestern United States. Journal of Vertebrate Paleontology 23(3 suppl.):85A; Stocker, M., Parker, W. G., Irmis, R. and Shuman, J. 2004. New discoveries from the Upper Triassic Chinle Formation as the result of the ongoing paleontological inventory of Petrified Forest National Park, Arizona. Journal of Vertebrate Palaeontology 24(3 suppl.):118A.).
Each of these communicated, in advance of Parker's January 2007 paper in Journal of Systematic Palaeontology (a manuscript submitted in May of 2005), that Parker believed "Desmatosuchus" chamaensis was assigned to the wrong genus.
One of these (the thesis, a copy of which was sent to NMMNHS) actually proposed a name for the new genus to which he asserted the specimen properly belongs.
One of the papers where Parker asserted the generic separation was published in the NMMNHS Bulletin.
Not being a paleontologist, I cannot saw with certainty that being the first to claim in print "this critter has been assigned to the wrong genus" is sufficient to earn you the recognized right to name the new genus in question. However, it is fair to say that a good number of people in that scientific community seem comfortable saying the naming rights should follow from the recognition (and demonstration) that the existing name gets the critter's taxonomy wrong.
Moreover, there is more than ample evidence that Parker had communicated very clearly that the assignment of "Desmatosuchus" chamaensis was wrong.
Did Lucas and colleagues not know that Parker thought the assignment of "Desmatosuchus" chamaensis was wrong? By Lucas's own admission, he did know it.
Did Lucas and colleagues assume that Parker had no intention of naming the new genus? This would assume that they did not read the thesis that had been sent to the NMMNHS. While this is plausible, surely sending a copy of the thesis to the museum is at least an attempt to communicate the information contained therein.
Did Lucas and colleagues hold the view that being the first to claim in print "this critter has been assigned to the wrong genus" is not sufficient to earn you the recognized right to name the new genus in question? Their actions would make it seem so.
The wording of the International Commission on Zoological Nomenclature's International Code of Zoological Nomenclature Code of Ethics (Appendix A, item #2) is as follows:
A zoologist should not publish a new name if he or she has reason to believe that another person has already recognized the same taxon and intends to establish a name for it (or that the taxon is to be named in a posthumous work). A zoologist in such a position should communicate with the other person (or their representatives) and only feel free to establish a new name if that person has failed to do so in a reasonable period (not less than a year).
What counts as "reason to believe that another person has already recognized the same taxon and intends to establish a name for it"? Lucas et al. had reason to believe Parker had recognized a new taxon -- they cited the 2005 Parker and Irmis paper to that effect. Did they have reason to believe that Parker didn't intend to establish a name for it? Did they contact him to ask?
Meanwhile, on the committees claim that Lucas et al. should have communicated to Parker that he was not to publish on their specimens while "under study", I'll defer to the comments of paleontologist Kevin Padian as to why such communication might not have transpired:
I disagree that Parker needed to get permission or to inform Lucas
et al. in advance of his taxonomic conclusions. They had already published theirs on several occasions. Every qualified worker has a right to access to published specimens to check published conclusions, and to come to different ones as the case may be. That's how our science tests its hypotheses; you can't do it any other way.
As I read this, Padian is claiming that publishing your taxonomic conclusions communicates an official opening up of the conversation about those conclusions within the professional community. That Lucas et al. had published on the taxon in question meant that it could no longer be construed as under their exclusive study. In some sense, an additional contact in which they told Parker, "Sorry, we're still working on these, so you'll have to hold off," would have been a contradiction of what their publications had already communicated to the professional community at large.
Indeed, one gets the sense that sometimes workers within the professional community might be trying to hedge their bets by purposely making what is communicated ambiguous. Certainly, if communication demand more than publishing and sending copies of relevant works to the person with whom you're trying to communicate, it is hard to know what else can be reasonably demanded. Must you read your articles aloud, over the phone or in person, to him? What if his attention wanders while you are reading to him?
If the official means by which knowledge is communicated is the peer reviewed literature in one's field, it should not be too much to expect that members of that professional community will at least try to keep up with it.
6. ...except when too much communication leads to problems like these.
[T]he expectation that theses and dissertations that have not been republished in widely read periodicals will be read by most workers or manuscript reviewers is unlikely to be realized. If students publish material in theses or dissertations that they intend to republish in other venues, they should be wary about circulating their work until publication is well under way, if they are concerned that their work is topical enough that other workers might want to draw immediately from their findings. Conversely, those who are aware of the results of an unpublished thesis should allow the thesis writer a reasonable amount of time to publish his or her results first, even if similar results are obtained independently.
Doesn't this point seem to be in tension with the exhortation for more communication between independent workers within the community of paleontology? Here, there seems to be a clear recognition that what you communicate to others can be used against you in the race to get across the finish line first -- especially if you are the writer of a recent, topical, not-yet-published thesis (which is to say, a junior person in the professional community). On this, Kevin Padian notes:
It is expected that students will publish the results of their theses, and so when Martz sent a copy of his to Lucas et al. as a courtesy, he was effectively notifying them of the completion of his work and the implicit intent to publish. In hindsight, they should at least have checked with him before publishing virtually all the conclusions of his thesis and arguing with them. The EC's view that students should be "wary about circulating their work" until it's almost published seems to acknowledge that there are sharks out there, and it comes close to blaming the victim. I'm concerned about the effect that statements like that may have on younger workers.
(Bold emphasis added.)
The phrase "those who are aware" strikes me as being too vague here, given that Lucas et al. have rested their defense to these charges (as well as to the allegations made by Jerzy Dzik of the Palaeobiology Institute at the University of Warsaw) on a certain lack of awareness or understanding. I'd be much happier with some indication that a certain baseline level of awareness is, arguably, one's responsibility as a member of a professional community. Willful ignorance may be strategically useful, but only if one has decided that winning the individual competition is more important than being part of the collective effort to build good scientific knowledge.
Knowledge-building efforts require communication of findings and conclusions between scientists in the community. They also require the training and integration of new generations of scientists. Given that senior members of the community have the resources and connections to win the race to the finish line if they decide to, there seems no earthly reason a junior person should ever communicate anything but a published finding to a senior person. And yet, this rational survival strategy undercuts the communication that would benefit the community as a whole (in terms of building good knowledge) and the communication the SVP committee urges in lesson #5.
7. The role of the Internet.
[T]he public posting of opinion and correspondence about these allegations on the Internet has not been helpful to resolving these matters, both in regard to the SVP Ethics Education Committee fairly resolving the matters, but also in that it has potentially polarized and biased the vertebrate paleontology community in a way that jeopardizes fair consideration of these matters as a community.
Did the Internet have an effect on who knew about this case, who was discussing it, and how those discussions went? It seems quite likely.
Is this a bad thing?
Geologist Chris Rowan says:
Call me a cynic, but I rather suspect that without the publicity, there probably wouldn't have been any sort of inquiry, and there would have just been a couple more sad and anonymous entries onto the list of junior researchers who feel that they were screwed over by their elders and supposed betters. Furthermore, at least for my part I have studiously avoided passing judgement on the allegations themselves, and focused more on how they were being handled. I've seen far too many complaints get ignored or brushed off with a "that's just the way it is", to trust that they'll be seriously considered without a bit of nudging.
The inquiries into the potential misconduct of Spencer Lucas and others by the DCA were biased and unfair and the coverage of the story on the internet prevented the controversy from quietly slipping away or being forgotten. It was recognized from the beginning that the results of this case would have the potential to change various aspects of the way professional paleontologists carry out their work and therefore it should have gotten all the attention it was due as the events of the case unfolded.
And paleontologist Kevin Padian says:
I don't agree that internet postings made it more difficult to assess the case. The documents received by the EC were all that they could and did act upon. Without the internet postings the incidents would have gone quietly away. Now, at least, there is a chance for broad education, which will for the first time be part of the SVP meeting in the Fall.
The types of conduct alleged in "Aetogate" are not mere offenses against individuals. Rather, they are crimes against the professional community, its common work, and its shared values. The resolution of these cases is not just of interest to the principals involved, but to the whole community -- a community which needs to know whether certain of its members are or are not trustworthy, whether certain "obvious" but unspoken expectations are really so obvious, whether certain practices have the net effect of nurturing or harming the community's newest members.
It is also worth pointing out that while the old guard of a professional community like paleontology has a well established network of real-life contacts, maintained at meetings and via phone calls and in the literature, the newer members of the community make great use of the Internet in building their own professional networks. (Undoubtedly, it has also been instructive to the newer members of the community of paleontology to see, by the magic of the internet, the range of reactions to "Aetogate" from the senior members of their community.)
Arguably, having the whole professional community involved in the discussion -- not just about particular allegations, but about the proper balance between competition and cooperation -- is a good thing. It ought to be the practitioners of that field, rather than a small subset of them on the SVP committee, that actively engage with the question of what kind of professional community paleontology is to be.
*A very smart researcher in chemical education (though precisely which one I cannot remember) made the point that what we want students to learn had better be something we actively assess, because students will set themselves to actually learning what they'll need to do well on our tests and assignments. My hunch is that professional scientists, like students, take most seriously the standards that are actually reflected in reward (or penalty) structures, not the ones about which nicely worded statements are promulgated.
Some questions arise:
1. To what extent is an author expected to do his/her "homework" (specifically a search for relevant published work on the same or related subjects) before writing and submitting a paper for publication?
2. In relation to my question 1, since a dissertation is accepted by a committee of professionals in the field and an abstract of it is published in the easily available Dissertation Abstracts, shouldn't that dissertation be considered as de facto peer reviewed and published?
3. Who, if anyone, decides what publications in a given field are properly peer reviewed? Wouldn't it make sense to "accredit" journals in the same way we accredit degree granting institutions? Then it would also be possible to suspend or revoke certification of journals from the accredited list if they fail to meet acceptable standards of peer review. Even as it stands today, I'm sure that few, if any, reputable paleontologists will be willing to submit papers to the NMMNHS Bulletin unless and until they demonstrate a commitment to proper peer review.
To what extent is an author expected to do his/her "homework" (specifically a search for relevant published work on the same or related subjects) before writing and submitting a paper for publication?
In effect, there is no limit to how much "homework" a researcher is expected to do. This is something that comes out regularly in peer-review - a reviewer might ask why an author seemingly hasn't read or referenced publication X despite its vague relevance. If Parker had published abstracts, etc. on Desmatosuchus, it is not an excessive expectation that another author writing on Desmatosuchus should be at least aware of his existence.
Theses are a little more of a grey area, because a thesis is not necessarily distributed outside the institution where it is submitted. However, in Parker's case it seems a copy was sent to the NMMNHS. It is also generally considered good ethical practice for authors to send a copy of all publications that refer to material in a museum's collections to that museum - again, requirements for theses are a little more vague, but short papers would definitely apply.
In relation to my question 1, since a dissertation is accepted by a committee of professionals in the field and an abstract of it is published in the easily available Dissertation Abstracts, shouldn't that dissertation be considered as de facto peer reviewed and published?
This relates to questions of availability. The abstract of the thesis is certainly published, but the thesis itself may not be widely available. The thesis is not necessarily peer-reviewed - that depends on how the thesis was composed.
Who, if anyone, decides what publications in a given field are properly peer reviewed?
There's no actual "accreditation" of peer-review as far as I know, but a respectable journal would have its review protocols freely available somewhere (often published with the "Instructions for Authors" in each journal issue) and so open to critique. Peer-review processes may vary within the journal itself - Proceedings of the National Academy of Sciences of the USA, for example, has stringent review processes for research articles, but also publishes invited editorials by leaders in the field that may not be peer-reviewed as such.
At the risk of somewhat shamelessly self-promoting, I wouldn't mind getting some criticism on a post I've just written about this affair on the question of the right to publish.
oh yeah, that blame-the-Internet thing was priceless. Don't shine any light on anything, we'll all just take care of it quietly behind the curtain. Yeah, that always goes well.
Why does this thing remind me of the end of a bajillion Scooby Doo episodes where the museum director who has been revealed as the miscreant in the mask whines about "those meddling kids"???
I agree that 'winner-takes-all' incentive mechanisms usually have very negative consequences, not only in science but in other places (where it is perhaps even more difficult to prevent their arising; think about great piano performers: how many records do those in the second line sell, as compared to those in the first line?).
So we should think hardly on alternative mechanisms... or perhaps scientists themselves have already thought. [For example, the 'least publishable item' strategy works more or less against the 'winner-takes-all' mechanism, by dividing "one" discovery into many pieces, so that, in principle, each of them can be 'won' by a different scientists.] But other ideas are needed.
One possible ally here should be the branch of economics known a 'mechanism design' (cf. my paper http://www.uned.es/dpto_log/jpzb/docs/INFERENCE.pdf). I have tried to persuade economists of working on these problem, but without much success.
I can't imagine how rapidly Columbia would be dealing with Prof. Sames' retracted papers and their causes if news of it hadn't been put on the Internet. (Three years and still counting?) For some time, the intertubes was the only place one could find out what was and had happened (or any information at all).
Blaming the Internet for lack of collegiality when someone is caught professionally screwing their coworkers is like a "Stop Snitching" T-shirt, and deserving of the same response ("You stop hosing your coworkers in secret and we'll stop telling them about it.") The "we'll deal with this quietly behind closed doors" routine only works in Clancy novels (for a given definition of "works").
Not being a [bi]ologist, I cannot saw with certainty that being the first to claim in print "this critter has been assigned to the wrong genus" is sufficient to earn you the recognized right to name the new genus in question.
In terms of ethics, yes. In terms of the ICZN, not at all. The ICZN works more like Master Yoda: "There is no try. Only do." Either you name the genus (which Parker did at an entirely appropriate speed, given the insane lag between final acceptance and publication of his manuscript -- unfortunately, while at the upper end of the range, said lag is entirely normal), or someone else does.
The wording of the International Commission on Zoological Nomenclature's International Code of Zoological Nomenclature Code of Ethics (Appendix A, item #2) is as follows:
That said, the Code of Ethics is not part of the uppercase-R Rules. It is part of the Recommendations. Note the use of "should not" rather than "must not" or "cannot" or (most realistically) a wording like "a name published under such circumstances is invalid".
In other words, unless I have overlooked a Gigantopithecus in this room, Lucas & colleagues blatantly violated the Code of Ethics, and the somewhat ugly and unimaginative name Rioarribasuchus is valid anyway.
seems to acknowledge that there are sharks out there
Interestingly, it also seems to acknowledge that Lucas et al. are such sharks, though it doesn't explicitly say it.
Who, if anyone, decides what publications in a given field are properly peer reviewed?
Keep in mind that peer-review is not required by the ICZN.
(It will be required by the PhyloCode, though.)
There's no actual "accreditation" of peer-review as far as I know