Tutorial 12: How to find problems to work on

February 3, 2011

Millions long for immortality who don’t know what to do with themselves on a rainy Sunday afternoon.

–Susan Ertz, Anger in the Sky

If you’ve been following the past few tutorials, you now know how to get copies of academic papers (learn Google fu and ask politely) and how to become a paleontologist (write and publish papers). But what are you going to write and publish papers about?

My own experience, and my impression from talking with many others, is that when you move into a new field for the first time, it often  seems like all of the good projects are taken. Or you’ll have what feels like a great idea for a project and then find out that Romer already solved that problem back in the middle of the 20th century. My advice is going to seem trite, but it’s worked for me several times and it seems to be what most other people do as well. Are you ready?

Step 1: Work on something

Seems obvious, right? Of course you have to work on something. You can’t just be a generic scientist (the idea is attractive, but that occupation closed about four centuries ago), and you can’t accumulate papers on everything. You need a focus. But if you’re just starting out, how do you know what to work on while you decide what to work on? It’s a Catch-22.

There are basically two solutions: work on something that appeals to you, or let someone else pick something for you.

Don’t discount the second path. It’s a big benefit of having an advisor who can provide you with a starter project. I didn’t have any particular fascination for sauropods before Rich Cifelli put me to work on what would become Sauroposeidon; I fell in love with them along the way (Buddhists would call this my awakening). As far as I can tell, Mike took the first path, and started working on sauropods because they seemed cool, and fell more deeply in love with them along the way.

I don’t describe this as “falling in love” lightly. That’s what it feels like: a positive feedback loop wherein the more you engage with a subject, the more you enjoy engaging with it, and so on. A few rounds of that and you may find yourself in a committed relationship, also known as a “research program”, because that’s how you maximize your time with the object of your affection.

You may not fall in love with your first project. It might crash and burn. You might not even finish it. It’s really just there to be your runway, to get you up in the air and flying under your own power. One way or another, you’re going on to something else. If you get a paper or two out of it along the way, that’s gravy.

Some people may find all this talk about falling in love overwrought or goofy, and some people may not feel that way about what they work on. If that’s you, you have my full sympathy, and my advice is to keep trying new things until you find something that you really do fall in love with. It’s worth it. Also note that I am using the word “love” to mean something involving commitment, investment, and self-sacrifice, as opposed to infatuation; find something that gives you satisfaction, not merely pleasure.

The point of working on something, as opposed to taking a more general approach, is not just to cut the problem of becoming a scientist down to a manageable size. It’s also to give you some traction with real data and real arguments. If you tried to become a generic paleontologist, you’d have to fly at such a high level that you couldn’t afford to get engaged with the details of any one particular problem. If you go that route you will never “drill down” enough to make a useful contribution; you may become a very well-informed enthusiast, but you won’t be  a very productive researcher.

Step 2: Learn lots of stuff

“Data! Data! Data! I cannot make bricks without clay!”

— Sherlock Holmes, “The Adventure of the Copper Beeches”, by Sir Arthur Conan Doyle

Once you have a direction, even a vague and temporary one, you have to accumulate clay. The clay comes in the form of facts, hypotheses (tested and otherwise), ideas, suggestions, and so on, and you get it mostly from reading papers.

You need clay for two reasons. First, you simply have to have a foundation of knowledge before you’re going to be able to contribute anything. Furthermore–and this is the step that seems to trip up many who aspire to contribute–you really need to have a handle on where the field is right now, and how it got there.

It’s pretty common for internet cranks in general, and absolutely pandemic for dinosaur cranks in particular, to argue that Ivory Tower so-called experts are all blinkered by orthodoxy and that outsiders with no technical training are better suited to having the big ideas because they are unshackled by the weight of knowing all that has gone before. These people are almost always wrong, because they keep reinventing the wheel, and the wheels they reinvent are often square. Either they’re solutions to problems that have already been solved (behind the state of the art), or solutions to problems that don’t exist (they misunderstand the state of the art), or, more rarely, solutions no one could implement because the methods or evidence just aren’t good enough yet (too far ahead of the state of the art). A good idea for a project has to be testable, but so far untested. Which means that if you want to make a useful contribution, you have to catch up with the cutting edge, and then stay caught up.

If you trust yourself and believe in your dreams and follow your star, you’ll still get beaten by people who spent their time working hard and learning things and weren’t so lazy.

–Terry Pratchett, The Wee Free Men

It’s not a trivial amount of work, and it requires some humility. Rich Cifelli put me to work on what would become Sauroposeidon in the late spring of 1996, and we had a paper ready to submit in the late spring of 1999. Thanks to Brooks Britt and Kent Sanders, I started CT scanning and really thinking seriously about sauropod pneumaticity in 1998, and the major papers that came out of that were written in 2001 and published in 2003. So both of those major steps required about three years of work from inception to submission (and an additional year or two until publication). Not all of my papers have three years of work behind them, because as you progress you learn stuff that applies to more than one project and you get better at figuring out what you need to know to complete a project; the earlier ones involve more faffing about. But if you’ve never published, it wouldn’t be a bad idea to mentally prepare to spend a few years getting up to speed.

That’s another benefit of doing a formal degree program that Mike didn’t mention in Tutorial 10: it gives you some protected time in which to get up to speed. You can do it without doing a formal degree program. It will require more effort on your part, since you won’t have an advisor to guide you or fellow students to challenge you (although you may be able to find substitutes). But there’s no reason why it can’t be done.

Step 3: Think about things

When Newton was asked years later how he had discovered his laws of celestial dyamics, he replied, “By thinking of them without ceasing.”

— Timothy Ferris, Coming of Age in the Milky Way

This seems like the easy step, when you’re considering it at one remove, either because you haven’t plunged in or because you’ve already learned to swim. After all, what could be more fun than thinking about dinosaurs (to pick an example completely at random)? But when you first start pulling the clay together, it seems like all the good ideas have been taken, like everyone else in the world is working on something 100 times cooler than anything you could ever think of, and that you will surely be doomed to work only on the most trivial problems because you’ll never have any really good ideas.

(Aside: if you have loads of what seem like really good ideas, then either you have already grown through this stage, in which case get back to work, or you skipped Step 2, in which case I’ll be happy to talk with you–in about three years.)

Fear not, because as long as you keep at it, you are going to have good ideas. In fact, pretty soon you’ll be drowning in them, and it will happen a lot sooner than you think. And I’ll tell you exactly how that’s going to happen.

At first, you don’t know anything, and it seems like all the good ideas are taken, but that’s because you don’t know anything. But as you catch up with the cutting edge, you will start to notice holes in the fabric of science: things that no one has done before, ideas that haven’t been tested, established “facts” that seem a little wonky or that have been upset by new discoveries. Now you’re getting traction. Not all of these holes are going to be worth patching. As you learn more (Step 2 again, forever and ever, world without end), you may find that some things haven’t been tried because they’re just intractable, and that some established facts only seemed wonky because you didn’t fully understand them (beware–this happens a lot). So stay humble, and keep learning, and keep thinking.

By “thinking” here I don’t mean simply staring off into space (although that is sometimes a symptom of deep thought), or sitting down with a notebook and pencil and deciding to think, although that can be a useful exercise now and then. It’s more along the lines of living and breathing your work. You have to engage with your subject material on a deep level. It will become what you think about in the shower. It may even invade your dreams. This is what I meant up above when I described it as “falling in love”. When you fall in love with someone, it’s almost impossible to think about anything else. With any luck, you’ll find a problem that occupies your mind similarly, at least for part of the day. I wrote the GDI tutorial when I was doing a lot of mass estimation for a couple of upcoming projects, and I found that I was mentally rotating volumetric models of Plateosaurus in my head on the drive home  from work. Often I went to sleep with visions of translucent 3D sauropodomorphs dancing in my head.

At some point you are going to go through what I call the Big Flip, where the exponentially rising curve of your knowledge passes the exponentially falling curve of your perception of how much science has actually been done. As you attain some level of mastery of the field, you won’t see just a few holes in the fabric of science, you’ll see that science is mostly holes, and that what we know is tiny compared to what we don’t know, about just about everything. At that point, you’ll see potential projects everywhere you look. The problem then becomes not thinking of a project to work on, but deciding what to pursue from among the almost limitless array of things that you could work on, and that’s a problem for another tutorial.

Maybe. Neither Mike nor I have been active long enough to tell if we’re any good at sorting projects, and Darren is no help because his “solution” is simply to work on everything. About the only thing I know for sure is that sometimes you have to start a project to find out that it’s not worth finishing. Don’t feel bad about hopping off a project like that onto another, more promising one (to a point; you’re going to have to settle down and work sometime). Some projects actually get to the moon, and others burn up in the atmosphere, go into dead-end orbits, or blow up on the pad. Sometimes the only way to find out which is which is to strap yourself in and light the engines.

Surely, you think, I’m exaggerating about the “almost limitless” array of things to work on. But I’m not. Just as big-S Science is dwarfed by big-I Ignorance, pretty soon your own completed science will fall far behind your own potential science, and it will never catch up. Right now I have about a dozen published papers, and 35 folders on my hard drive for projects I have taken seriously enough to start working on. A handful of those will be published in the not-too-distant future, a few more are things I might work on after that, and the vast majority are things I’ll never get around to. Everyone I know who is active in science feels exactly like this (Darren Tanke has “about 55 writing projects on the go”, by his own count). In fact, one sign that you’ve had your Big Flip is when you look around at all of the stuff you have going on and realize that you are going to die with a lot of work left to do, whether that’s tomorrow or a century from now. When that realization hits, don’t despair. It means you’ve arrived. Dive into whatever looks the most promising at the moment, and vamp till fade.

Step 4. Be open

If we knew what it was we were doing, it would not be called research, would it?

–Albert Einstein

I can tell you from experience that parents with infants are hyper-alert, because they don’t want to drop their babies. For the first few hours and days, this alertness is almost exhausting. It’s like when you first learn to drive and you’re constantly twitching the steering wheel. Eventually you learn how to be hyper-alert and still do other things. The “don’t trip on that rug/avoid sharp corners/be prepared to fall on your back” program is still running, but you can have other windows open on your mental desktop. Evaluating the potential hazards in whatever space you’re in becomes reflexive.

When I say, “be open”, I’m talking about cultivating an alertness of that kind. Your research program will be running most of the time, even it it’s minimized or in the tray while you do other stuff, and it will constantly evaluate the facts and ideas you encounter and see if they fit. The other part of being open is feeding your brain a cosmopolitan diet. Inspiration comes from the most unpredictable sources. There’s no way to force inspiration to happen, but you can improve the odds by deliberately seeking out the unfamiliar.

There is a great bit in one of David Quammen’s essays in which Quammen is roaming the Montana State University library and he comes across Jack Horner sitting on the floor between two rows of shelves with journals spread out all around him. Quammen says, “Hey, Jack, what are you doing here?” Horner looks up and says, “Having ideas.” The best part is that the journals weren’t even paleo journals, they were ornithology journals. (Note to DMLers: including a positive anecdote about Jack Horner is an intelligence test. Try not to fail.)

The downside of deliberately seeking out new stuff instead of staying with the bounds of your research program (the Sofa of Science!) is that it will make you feel stupid. It doesn’t matter what line of work you’re in, whether it’s paleontology or programming or construction, there is something that you are an expert on now that you weren’t when you started, whether it is taphonomy or recursive subroutines or pouring concrete. But you weren’t an expert when you started, and when you started you probably spent a lot of time feeling stupid. But you learned quickly, partly because you were anxious to get past feeling stupid, and partly because trying dumb stuff is a good way to learn what works and what doesn’t. If you’re not feeling stupid, you’re too comfortable, and it might be time to do an audit and see if you’re actually contributing to science at all. Science requires a certain kind of stupidity (Schwarz 2008).

And once you’ve got a research program, it’s all potential grist for the mill. Throw facts and ideas in the air and see where they land (the whole idea is that you can’t predict that in advance). Some will land behind the cutting edge, some too far out in front, and some entirely off the map. But one or two might land on the cutting edge, or ideally just ahead, and then you can push the whole field forward, just a little bit.

Conferences are valuable because they give your mental program a huge slug of input. You don’t get sprinkled with new facts and ideas, you get carpet-bombed, and as the volume of fire increases, so do the chances for a successful hit. I got an idea for a sauropod neck paper from a talk on the foot morphology of perching birds at ICVM last summer. Another long-delayed project was inspired by a talk on the development of snail shells by a fellow grad student back at Berkeley. That’s one reason I like smaller conferences like SVPCA, with no concurrent sessions. If everyone is in one room, you’re bound to sit through talks you wouldn’t see otherwise, and those are where you’re most likely to get fresh ideas. At SVP I always opt for the dinosaur talks over the mammal talks, and that’s good for Step 2, but bad for Step 4, because I already know what most of the dinosaur talks are about. I’m adding a little clay, but possibly losing out on a lot of inspiration. If I was really taking my own advice, I’d go see the fish talks.

So, conferences are good, but really they’re just an intense version of something you can do all the time, which is choose to feed yourself new things.

Coda: Publish

“I was on an [email] list with Tom Clancy once.  Mr. Clancy’s
contribution to the list was, ‘Write the damn book’.”

–Greg Gunther.

I know Mike used that quote before, but it bears repeating.

This tutorial is not aimed at everyone. It’s aimed specifically at people who were inspired by Tutorial 10 but don’t know where to start. Well, now you know. Step 1 is a choice. Steps 2, 3, and 4 are habits to be cultivated, for the rest of your life. But you can pick a project, read all the papers you want, think about your topic constantly, and drench yourself in the rainstorm of new ideas, and none of it counts until you publish. It may be a great way to pass the time, it may be tremendously rewarding, and you may develop as a person, but it won’t be science until you communicate it in a form that other people can use (i.e., papers, not mailing list posts–you dino folks know who I’m secretly addressing).

Write the damn paper.


Disclosure: a couple of passages in this post are cribbed from the never-completed series, “Blundering toward productivity”, on my old blog. That series was a straight up pastiche of Paul Graham, but it includes a few more relevant ideas and might be of interest. Part 1, Part 2, Part 3, Part 4.

Finally: I can only link to things, I can’t put a gun to your head and force you to read them. But if I could, I’d make you read Schwarz (2008) first–it’s one page, and it’s important. After that, I’d make you read all the linked Paul Graham essays. If you have time to slog through my blatherations, you have time to read the better stuff that inspired me.

Update 2014-03-16: This post inspired a follow-up, and this much later post touches on some of the same issues.


Schwartz, M.A. 2008. The importance of stupidity in scientific research. Journal of Cell Science 121:1771.

39 Responses to “Tutorial 12: How to find problems to work on”

  1. […] Sam W is a post by Matt Wedel at SV-POW! (Sauropod Vertebrae Picture of the Week). It’s on “How to find problems to work on” and is part of a longer tutorial series on basically everything the folks at SV-POW can think […]

  2. David Hone Says:

    All in all that’s brilliant Matt. Great quotes too (I’ve used the Holmes one myself before). All of that is excellent advice and the Schwartz paper is great. Too few people I think, appreciate how hard research can be (I hesitate to say ‘is’ some things are quite simple).

    And as for projects, by my count I have 41 on the go right now, plus various abandoned ones and those that will surely die or are on semi-permanent hold. And for ideas, I keep a file on my desktop of things I could do. Every time I have an idea for a project I write it down so I won’t forget and years later it might get used or feed into something else.

  3. […] of friends, Matt Wedel has just posted one of the best things I’ve ever read on any blog: How to find problems to work on.  I strongly encourage you to go and read that brilliantly insightful piece, if only as an […]

  4. Casey Says:

    I really like the “Big Flip”, Its a great concept and I think it represents almost a catharsis during one’s education. Besides the “working on everything” solution, which does not work for me, despite my persistence in trying; howabout some wisdom on Choosing which research program to pursue? SVPCA is sounding appealing.

  5. ReBecca Says:

    Great post Matt. Is step 4 also promising that it is possible to do research after having a baby? ;)

  6. Matt Wedel Says:

    Is step 4 also promising that it is possible to do research after having a baby?

    It is. I promise. And congratulations!

    Funny story. A couple of weeks ago we had some friends over for dinner, including Andy Farke and his wife, Sarah, and Ilsa Lund, who at the time was on solo baby duty since Brian was off in the field. After dinner we were talking about being productive even when you’re busy. I don’t remember the specific lead-in, but at one point I loudly declaimed, “No-one knows how to manage their time until they have their first kid anyway.” And only then did I remember that Andy and Sarah haven’t had kids yet. Fortunately, we all had a good laugh at my expense, and I went looking for a crowbar to see if I could pry my foot out of my mouth.

    So, although I am not making that claim here, Halfway Drunk Matt From Two Weeks Ago thinks you might be even more productive in the future.

    Present Matt says don’t worry about where the ideas will come from. As a new parent, you’re about to discover the whole world over again. Treasure it.

  7. […] Millions long for immortality who don’t know what to do with themselves on a rainy Sunday afternoon. –Susan Ertz, Anger in the Sky via […]

  8. […] Sauropod Vertebrae Picture of The Week on how to find problems to work on […]

  9. ReBecca Says:

    Thank you! I keep trying to remind myself that she will only be a baby and this tiny once and I should just try to enjoy every moment of it while I can. Its hard to try to find time to even read a paper, let alone work on research. Seems a little easier for John. At least we have one paper in the tubes, just need to get back on several more.

    That is a funny story. Something tells me Andy and Sarah will be just as productive as they are now after they have their first kid. I will take the advice of both drunk and sober Matt. Thanks, its good to know ;)

  10. Andy Says:

    My productivity is something of an illusion – having my spouse in a different state most of the time sadly means more research gets done!

  11. […] Sauropod Vertebra Picture of the Week: Tutorial 12: How to find problems to work on […]

  12. 20tauri Says:

    If only all aspiring scientists would read this, there might be a lot more sci students and postdocs sticking it out past the rough beginnings… Thanks for sharing! I’ll be sure to reference this (and the Schwartz paper) in the future.

  13. Nathan Myers Says:

    Yeah, thanks a lot, Matt: more competition for grants.

    :-) Excellent. With a bonus quote from Terry Pratchett! Anybody’s ten-year-old needs to see Wee Free Men. There are three sequels. Unlike every other writer’s, Pratchett’s sequels just get better and better.

  14. Zach Miller Says:

    Thanks for this, Matt. Your “how to” posts have been great inspirations to me, and I’m happy to say that I’m currently outlining two different projects for (hopefully) future publication due in no small part to these inspiring posts.

  15. “…for internet cranks in general, and absolutely pandemic for dinosaur cranks in particular…”

    Advice on cranks, from an orthodox subscriber to the dead field of dinobird palaeontology. (Though he isn’t a bird-evolutionist, the point is, he’s still a palaeontological cliquist, as we shall see.)

    And we need not doubt that I am seen by him as a crank; he and his have never once shown any appreciation or positive recognition of anything I’ve offered over the years, whatever it’s nature, and never will. (They obviously see me as some kind of multi-dimensional nutter.) How do I fulfill Wedel’s criteria?

    “It’s pretty common for internet cranks in general, and absolutely pandemic for dinosaur cranks in particular, to argue that Ivory Tower so-called experts are all blinkered by orthodoxy and that outsiders with no technical training are better suited to having the big ideas because they are unshackled by the weight of knowing all that has gone before.”

    Let’s look at my areas of “inexpertise”. Most of the inverted pyramid of criticism I make rests on cladograms, (computer-generated family trees) and the way Wedel et al. unquestioningly trust them (while usually denying it). As my masters was in “information systems engineering”, and it dealt with a fair bit of the stats and maths of designing and running programs and understanding their outputs and, importantly, inputs, it would be a terrible waste of (public) money if I hadn’t picked up a reasonable background on computer-generated anything. I’ve got other useful related experience I hope I’ll resist wheeling out here. When Wedel and his like behave as though you can never second-guess a cladogram structure, and then roll their eyes and claim special understanding when I point to violated conditions for trusting that cladogram, and to examples of known untrue cladograms, they cannot claim I have “no technical training”. Since Wedel himself has neither any notable formal training in that area which is central to the science, nor impressive experience in it, his superior attitude is unjustified if directed to me. There are others he will listen to who have comparable background to mine, but they above all should know better than to brand anyone who doubts a cladogram, as a crank. (Fact is, the really useful research towards detecting validity levels in cladograms, and detecting what invalid ones really should be saying, is what the “so-called experts” would be doing if they knew their job, and they’re not. If they were experts they wouldn’t mistake metrics such as consensus, bootstrapping etc as convincing confirmation of validity, as they so often do.)

    Another rarely mentioned but telling point is the assumption that a once-through approach is the best way to analyse the data put into cladograms. For many problems it’s best to progressively refine solutions by going over the same data again and again. This “iterative” approach can often be used when there isn’t a neat solution, and in fact there isn’t to most complex problems. That’s why the brain sends feedback from later stages in the visual system to earlier ones. Not only is a once-through solution unlikely to be the best for combining bone shapes, palaeogeography, time, etc, but in fact, the family tree, the causes of detailed evolutionary events, understanding of ancient connectivity between continents, are all best solved together. This is well understood by those dealing with processes of complex understanding, and they know it because of their experience of systems performance in engineering, the design and processing of brains, etc. These are fields I’ve had enough contact with to be able to say categorically that the simplistic once-through, and ‘phylogeny first and everything else later’ approaches are simply due to basic ignorance in the states of the ‘arts’ involved. That just isn’t negotiable until a critic shows they’ve understood the vital lessons from related disciplines and explained why they can’t apply.

    So, in the most important area, his sneer would make more sense reflected back at the likes of himself.

    Then there’s the fallacy of “experience” without feedback. Those skeptical towards religion and astrology understand immediately that no matter how many thousands of years you’ve been doing something, if you don’t actually have any meaningful feedback that your activities genuinely “work”, then you haven’t had any real experience at all. It’s only too common for people to have been doing something for forty years or forty centuries, while doing it wrong all that time. The best depiction of this principle is when Adler pronounced on a psychological case Popper informally reported to him (see: http://www.oocities.com/strangetruther/pottedpopper.html ). Adler readily analysed the case in terms of his own theory even though he had never seen the child in question. Popper asked how he had been so sure of his analysis. When Adler replied: “Because of my thousandfold experience,” Popper couldn’t help saying: “And with this new case, I suppose, your experience has become thousand-and-one-fold.” Same with cladograms of long extinct creatures, unless you have that time machine. Science Is possible on them but only if you scrupulously stick to strategies proved useful in investigative fields that Do offer feedback.

    Then there’s just general background knowledge about anything. I’m constantly shocked by dinobirders, usually cladists, who seem to lack the intellectual hinterland suitable for science. They hang on desperately to their cladograms because without them they feel lost. They seem to have no idea that cladograms are just one implementation of “the search for the best explanations”. That principle underlies all science, indeed all knowledge, yet when they haven’t got a cladogram to hang onto, their next appeal is to simplicity/parsimony/Occam’s Razor as the basis of all science. Simplicity is one aspect of explanatory power; cladograms can be seen as looking for the simplest solution using some of the data. (Then there’s the whole “Just-So Stories” fiasco where one of Steven J. Gould’s many unfortunate comments is given huge importance despite that criticism diametrically opposing the basic Popperian principle of explanation – inevitably not even noticed of course.) Yet more scientifically essential aspects of just Popper’s vital teachings they’ve not taken on board.

    Reading Wedel’s talk about ‘cranks’ seems more childish and offensive every time I read it. His wonderful idea combines the forging of a pack of like-minded friends, while identifying outsiders we are advised to spurn, try to ridicule, and ignore without making any effort to understand them. It is actually a basic [compound of] instinct[s], and though gangsterism is useful to those doing it, even in science, it is also the opposite of true civilisation, and the enemy of science as a whole. Most people in the world are religious, and frankly, I’d take a creationist over a cladist most days of the week – denying science is more easily cured that corrupting it. But the religious would of course be cranks. In a few minutes though, I could find in any atheist some unscientific or stubborn belief or attitude that would qualify him as a crank, by Wedel’s lights – starting with Wedel himself. As a psychologist, I count his unpleasant exhortations either as victimisation of the unfortunate, but actually more like xenophobia. I don’t really mind that it’s the likes of me he thinks he’s talking about since anyone scientific from youth will be familiar with knowing most other people are mistaken, and oddly, it’s not the paradox that actually it’s his lot that are the cranks – it’s really the attitude more than anything else.

    However, it’s Really scientifically inadvisable. In psychology huge efforts are made to take account of non-relevant influences where necessary. Bias is a huge issue. There cannot be any justification for recommending listening most your friends; it’s a natural tendency you don’t have to recommend. Most problems with scientific advance come from people not listening, typically because they don’t like a person or a group, and they don’t like those who keep criticising… which has to be done because of the irrational reasons the wilfully ignorant find for not listening! And to get back to his paragraph I quoted at the beginning, his implication that “outsiders” (his term) should be treated as cranks, is an invitation to despise those attempting the already hugely difficult process of cross-discipline productivity. Inter-disciplinary fertilisation certainly finds plenty of resistance but at least most appreciate its value, and if he can’t think of numerous examples, that’s a reflection on him. Discussing with friends can be very useful but thinking on your own can actually be more useful, particularly for those whose minds have been open a long time. The trouble with favouring your friends is that you short-change others; it sounds so nice merrily co-operating with your friends – until you realise you’re poisoning science.

    In the light of this, Wedel’s comments from part 3 of his 2009 postings are particularly hypocritical:

    “…have at least a nodding acquaintance with every field that bears on yours.”

    It should be added that academic fields you are not acquainted with often seem pretty insane until you understand them. Palaeontology is a field you can just walk into and learn without being astonished; philosophy of science, reasonably advanced problem solving, and other relevant fields are not.

    “The downside of jumping into a new field instead of just soaking your toes at the shallow end is that it will make you feel stupid.”

    So often, because of a serious lack of humility in palaeontologists (see below), if someone familiar with a significant related field, or even sub-field to palaeontology, tries to explain an important error, Wedel and his friends will simply not believe that person can be so right when they are so wrong.

    And from his February 3, 2011 2011 SV-POW! posting “Tutorial 12: How to find problems to work on”:

    “It’s not a trivial amount of work, and it requires some humility.”

    Too true. Shame you skipped a relevant degree or two. Just like most of your friends.

    This isn’t the first, or the second, or even the third time I’ve had to deal with a huge pile of crap coming out of Berkeley.

  16. Mike Taylor Says:

    John, I wrestled with myself for some time before deciding to allow your comment through moderation — that I did is mostly just because you evidently put so much effort into writing it, and it didn’t seem right to let that go to waste. But your posting is borderline, consisting largely of personal abuse. I give warning now that I will not approve another comment this personal and abusive: if you have points to make on this forum, then please make them politely.

    As to the substance of your comment: it seems odd to me that you would self-identify as a crank, then take offence at comments made about cranks as though they had been made about you personally.

    Regarding professional palaeontologists’ attitudes to cladograms, I have to say that my experience has been overwhelmingly the exact opposite of the “unquestioning trust” that you describe. On the contrary, everyone who has generated cladograms through cladistic analysis is all too aware of how tentative and open to revision the results are: hence for example Paul Upchurch’s response on finding that Jeff Wilson’s sauropod cladograms disagreed with his regarding monophyly of “Euhelopodidae” and the position of Euhelopus. Rather than “fighting his corner”, he did what all good scientists do, and investigated the objective sources of the disagreement, resulting the joint Wilson and Upchurch (2009) paper on Euhelopus that resolved these issues. Yes, a cladogram, whether generated by a computer or otherwise, is only a working hypothesis. Everyone knows this; indeed, knows it so well that it’s taken as read, which is why that uncertainty doesn’t get lengthy discussion in every paper that contains one.

    Finally, if you’ve been reading our series of tutorials and come to the conclusion that we SV-POW!er Rangers are trying to exclude outsiders, then you have been reading them very differently from how we wrote them. We’ve sent a very strong and consistent message that this field is not open only to insiders, but also to avocational palaeontologists such as John McIntosh, Greg Paul and indeed myself. You just have to conduct yourself as a professional.

  17. Mathew Wedel Says:

    But your posting is borderline

    Just so no one else gets the wrong idea, it’s actually WAY past the borderline, and normally we’d mark it as spam and permanently block the sender. We like our civil little corner of the internet. But we’re letting this one stand because it so vividly illustrates my point; in sports this is called an ‘own goal’.

  18. David Marjanović Says:

    It should be added that academic fields you are not acquainted with often seem pretty insane until you understand them.

    That’s your own goal.

    There’s plenty of primary literature about cladistics and the computer programs for it. You don’t give me the impression that you’re familiar with it…

    If you think you can do better, fine, write a paper on this instead of whining on a blog. Just be aware that no journal editor will let you emphasize words by beginning them with a capital letter. <headdesk>

  19. Thanks for your reply Mike, and for your reason for passing my comment, though it’s served as a posting to my own blog so it wouldn’t have been wasted. Deducing other people’s identifications is not the same as making them yourself. I most certainly do not “self-identify as a crank”. It was no great leap to see that talk of ‘cranks’ would include me, justified or otherwise, and I don’t doubt I was right in my estimation. I note it hasn’t been denied. But if Wedel doesn’t see me as a crank I’d be a second category of those whose arguments are customarily dismissed without consideration.

    Pleased to hear your news that cladograms are not the be-all-and-end-all now, but it’s wrong. Unquestioning talk such as “analysis indicates that…” is still standard in many areas.

    Outsiders means non-co-theorists, not those not employed as palaeontologists.

    As to the field being open to those with different ideas, then this DML comment to Greg Paul:
    “…no authors are allowed by their editors to cite your work in peer – reviewed literature.”
    …and this by GSP himself:
    “I put in an abstract for an SVP talk but they reject me every year these days”
    …is as clear an indication as any that the field has died, since if he isn’t considered worthy of getting a fair shout, no-one with any new ideas is.

    Yet you talk as if nothing I said is justified.

    To Wedel:
    My comment vividly illustrates your point does it? Which point? That those who don’t treat you as a friend are cranks to be ignored? I’m sorry but when mistakes are wilfully repeated decade after decade you must expect anger. As your comment doesn’t attempt to address any of my points, it exemplifies your closed-mindedness to those who don’t approve of you, so further justifies disapproval of your approach. If you won’t listen to those who disapprove, you’ll feel fine about getting things wrong forever. If you want to insist you have to stay calm and complimentary all the time to be a scientist, you’ve missed the point that you can’t compliment a theory if you see that it’s wrong. You condemn yourself by pretending science is all about agreement, and implying that destructive stubbornness deserves no more than a smile.

  20. Mathew Wedel Says:

    My comment vividly illustrates your point does it? Which point? That those who don’t treat you as a friend are cranks to be ignored?

    You haven’t been banned from several mailing lists and blogs because your ideas are unconventional. People treat you like a crank because of comments like your own above, where instead of making useful arguments based on evidence, you hurl abuse at anyone who disagrees with you.

    As your comment doesn’t attempt to address any of my points, it exemplifies your closed-mindedness to those who don’t approve of you, so further justifies disapproval of your approach. If you won’t listen to those who disapprove, you’ll feel fine about getting things wrong forever.

    You seem to be confusing disapproval with the ability to disprove something. The fact that you disapprove of the conclusions I’ve drawn means nothing; science does not run on opinion. You must show with evidence why I am wrong and your interpretation is better.

    If you want to insist you have to stay calm and complimentary all the time to be a scientist, you’ve missed the point that you can’t compliment a theory if you see that it’s wrong.

    Please show me one place, on this blog or anywhere else, where I have ever insisted that people compliment my work. Again, you’re confusing personal approval with scientific worth. It doesn’t matter to me whether people compliment my work or not. All that matters is whether it fits the available evidence.

    You talk a lot about compliments, approval, friends, smiles, anger, and so on, and very little about evidence. It doesn’t help your case. In fact, it’s pretty pathetic.

    You condemn yourself by pretending science is all about agreement

    Uh, dude, have you read this blog at all? I disagree with people publicly all the time. But those disagreements are about more than personal “disapproval”, they’re about whether or not particular interpretations best explain the evidence. And even when I disagree with others about science, it’s at least cordial, and often friendly (see this, for example).

    You can disagree with me, disapprove of me, and call me names until the end of time, and no one will care. Unless you present the evidence to show why you are right and I am wrong, it’s just empty ranting.

    You’ve got a blog, so you can’t claim that anyone is censoring you. Please, show the world with evidence why I’m wrong and you’re right. Admittedly, that would involve some actual work, and not just name-calling. Let’s see if you’re up to it. Consider the gauntlet thrown down.

    (Oh, and you’re going to have to show this work somewhere else; we’re not going to engage in an endless battle of words with you here. Our lenience is swiftly nearing its end.)

  21. Mike Taylor Says:

    “You seem to be confusing disapproval with the ability to disprove something.”

    … or “confusing disapproval with disproval“, if you will.

    I’ll get my coat.

  22. “You haven’t been banned from several mailing lists and blogs…”

    That’s right.

    “…comments like your own above, where instead of making useful arguments based on evidence, you hurl abuse at anyone who disagrees with you.”

    My comment he refers to is below. See if you can spot the abuse:

    “You seem to be confusing disapproval with the ability to disprove something.”

    No, I’m not, as a clear reading of my words shows.

    I’m not commenting on the rest; the points I made haven’t been addressed. My advice now as before is don’t concentrate on trying to identify ‘cranks’ – the results up till now haven’t been good, and it’s the argument that counts not the person.

  23. Mike Taylor Says:

    Yes, it’s the argument that counts, not the person.

    Problem is, we’re still waiting for you to make one.

  24. Matt Wedel Says:

    My comment he refers to is below. See if you can spot the abuse:

    “You seem to be confusing disapproval with the ability to disprove something.”

    No, actually, I was referring to your first comment on this post, in which you wrote, “This isn’t the first, or the second, or even the third time I’ve had to deal with a huge pile of crap coming out of Berkeley.”

    Anyway, you’re confused about my goal. It’s not to identify cranks–you did that yourself, remember–but do actual work. Something that you have shown neither the willingness nor the aptitude for. But as I said before, please feel free to prove me wrong.

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