In praise of slow science

Its a rush rush world out there. We expect to be able to talk (or text) anybody anytime anywhere. When we order something from half a continent away we expect it on our doorstep in a day or two. We’re even walking faster than we used to.

Science is no exception. The number of papers being published is still growing exponentially  at a rate of over 5% per year (i.e. doubling every 10 years or so). Statistics on growth in number of scientists are harder to come by – the last good analysis I can find is a book by Derek de Solla Price in 1963 (summarized here) – but it appears the doubling time of scientists, while also fast, is a bit longer than for the doubling time of the number of papers. This means the individual rate of publication (papers/year) is going up. Students these days are being pressured to have papers out as early as their second year*. Before anxiety sets in, it should be noted that very few students meet this expectation and it is probably more of a tactic to ensure publications are coming out in year 4 or so. But even that is a speed up from publishing a thesis in year 6 or so and then whipping them into shape for publication which seemed to be the norm when I was in grad school. I’ve already talked about the growing number of grant submissions.

Some of this is modern life. Some of this a fact of life of being in a competitive field (and there are almost no well paying, intellectually stimulating jobs that aren’t highly competitive).

But I fear we’re losing something. My best science has often been torturous with seemingly as many steps back as forward. My first take on what my results mean are often wrong and much less profound than my 3rd or 4th iteration. The first listed hypothesis of my NSF postdoc proposal turned out to be false (tested in 2003-2004). I think I’ve finally figured out what is going on 10 years later. My first two papers did not come out until the last year of my PhD (thankfully I did not have an adviser who believed in hurry up science). But both of them had been churning around for several years. In both cases I felt like my understanding and my message greatly improved with the extra time. The first of these evolved from a quick and dirty test of neutral theory to some very heavy thinking about what it means to do models and test theory in ecology. This caused the second paper (co-authored with Cathy Collins) to evolve from a single prediction to a many prediction paper. It also lead to a paper in its own right. And influenced my thinking to this day. And in a slightly different vein since it was an opinion paper, my most highly cited paper was the result of more than 6 months of intense (polite but literally 100s of emails) back and forth debate among the four authors that I have no doubt resulted in a much better paper.

I don’t think I’m alone in appreciating slow science. There is even a “slow science” manifesto although it doesn’t seem to have taken off. I won’t share the stories of colleagues without permission, but I have heard plenty of stories of a result that took 2-3 years to make sense of. And I’ve always admired the people who took that time and in my opinion they’ve almost always gotten much more important papers out of it. I don’t think its a coincidence that Ecological Monographs is cited more frequently than Ecology – the Ecological Monographs are often magnum opus type studies that come together over years. Darwin spent 20 years polishing and refining On the Origin of Species. Likewise, Newton developed and refined the ideas and presentation behind Principia for over a decade after the core insight came.

Hubbell’s highly influential neutral theory was first broached in 1986 but he then worked on the details in private for a decade and a half before publishing his 2001 book. Would his book have had such high impact if he hadn’t ruminated, explored, followed dead ends, followed unexpected avenues that panned out, combined math with data and literature and ecological intuition and generally done a thorough job? I highly doubt it.

I want to be clear that this argument for “slow science” is not a cover for procrastination nor the fear of writing or the fear of releasing one’s ideas into print (although I confess the latter influenced some of the delay in one of my first papers and probably had a role with Darwin too). Publication IS the sine qua non of scientific communication – its just a question of when something is ready to write-up. There are plenty (a majority) of times I collect data and run an analysis and I’m done. Its obvious what it means. Time to write it up! So not all science is or should be slow science. Nor is this really the same as the fact that sometimes challenges and delays happen along the way in executing the data collection (as Meg talked about yesterday).

But there are those other times, after the data is already collected, where there is this nagging sense that I’m on to something big but haven’t figured it out yet. Usually this is because I’ve gotten an unexpected result and there is an intuition that its not just noise or a bad experiment or a bad idea but a deeper signal of something important. Often there is a pattern in the data – just not what I expected. In the case of the aforementioned paper I’ve been working on for a decade, I got a negative correlation when I (and everybody else) expected a positive correlation (and the negative correlation was very consistent and indubitably statistically and biologically different from zero). Those are the times to slow down. And the goal is not procrastination nor fear. It is a recognition that truly big ideas are creative, and creative processes don’t run on schedules. They’re the classic examples of solutions that pop into your head while you’re taking a walk not even thinking about the problem. They’re also the answers that come when you try your 34th different analysis of the data. These can’t be scheduled. And these require slow science.

Of course one has to be career-conscious even when practicing slow science. My main recipe for that is to have lots of projects in the pipeline. When something needs slowing down, then you can put it on the back burner and spend time on something else. That way you’re still productive. You’re actually more productive because while you’re working on that simpler paper, your subconscious mind is turning away on the complicated slow one too.

What is your experience? Do you have a slow science story? Do you feel it took your work from average to great? Is there still room for slow science in this rush-rush world? or is this just a cop-out from publishing?

*I’m talking about the PhD schedule here. Obviously the Masters is a different schedule but the same general principle applies.

28 thoughts on “In praise of slow science

  1. Thank you so much for this post, Brian. As someone who primarily works with generating data, rather than models or analyses of large pre-existing data-sets, I already feel as though I’m on the slow end! But your points really resonated with me as I have a couple of papers that I’ve been mulling, and which I’ve had the chance to present at a few conferences in the last couple of years. I know they’ll be better for my not rushing them (and the new perspectives from talking with outside folks) even as I feel the pressure to PUBLISH! PUBLISH! PUBLISH!

    I’ve also seen colleagues who do great, innovative work not get jobs because they publish slowly (but the papers are important and well-cited). It seems to me that raw numbers aren’t a great currency.

  2. This is a good follow-up to yesterday’s post on Science is Hard. After reading that, my first thought was, how do some ecologists have 15 to 20 (or more!) publications per year?

  3. YES! We all suffer because people need to push science out the door for career advancement (getting and staying employed, that is) when longer gestation times results in a much better and more valuable product.

  4. Brian, excellent post. I appreciate that you emphasize here that slow science can have it’s place well after the experiments have been designed and the data collected, and in non-empirical work as well. Like you say, sometimes the analysis and interpretation is straight-forward, but not always! I’m also a fan of the multiple-projects route; like you I’ve found it’s the only way I can give certain things the time they need to stew.

  5. We’re even walking faster than we used to?! That’s amazing!

    I totally agree that lots of projects in the pipeline is a way to allow for slow science and career progression.

  6. Brian’s captured how I operate, especially when I’m doing my best stuff. And I’ve never worried that it would cost me, career-wise, and it hasn’t. Paradoxically, I think the best way to advance your career often (not always) is not to worry about what will advance your career.

    And I don’t think Brian, Meg, and I are alone in this. Lots of good ecologists, including ones who’ve just been hired recently, operate more or less this way. You can easily verify this by looking at their cv’s and seeing that they have never published 10+ papers/year, not even after they had labs and began co-authoring papers with grad students and postdocs.

    I sometimes wonder if people overestimate the extent to which just having lots of papers actually advances your career.

  7. As for specific “slow science” stories, in comments and posts elsewhere I’ve mentioned that it literally took me 3 years or so of off-and-on work to *really* understand the Price equation. Along the way I had the pleasure of embarrassing myself in front of Alan Grafen, when I made the mistake of talking to him when I didn’t actually know yet what I was talking about (I thought I did, but I didn’t). It paid off–I consider my first paper on the Price equation (Fox 2006 Ecology) to be one of my three best papers.

      • Thanks, but I doubt it would’ve helped me. I had Price 1972, Price 1995, and Price 1995 in front of me all the time and worked through them very carefully and it still took me yonks to figure it out. And figure out how to “translate” it from evolutionary terms into biodiversity-ecosystem function terms (that was the hardest part). I leave it to others to judge how much that says about the Price equation, and how much it says about me.🙂

        And I confess I’m a little suspicious of any Price equation explainer that links to van Veelen’s work. On the evidence of his papers, van Veelen doesn’t really “get” the Price equation. I don’t mean that he makes technical mathematical mistakes, but the way he interprets it is in my view rather strange. He and Steven Frank have been fighting about this in the literature, and my own view is very much in line with Frank’s. Sean Rice’s work, and his homepage, is another excellent Price equation resource.

      • Hi Jeremy,

        I didn’t mean it in a bad way, I am a happy agnost. It is just that I came across the website about the same time as I read your comment, and decided it was a funny comment. It has made me very curious about it, the way some have opposite strong ideas about the concept. Still, it seems best for me to remain blissfully ignorant.

  8. There is a version of the Optimism Bias from cognitive psychology that predicts, no matter how experienced one is, one always underestimates the time to complete a project. Attempts at rationally dealing with the bias–like breaking down a project into its sequential parts and summing up the estimated times to completion for those parts–actually exaggerate the effect!
    I’m reminded of this because every time I think I have the data in hand and the paper outlined in my head, I dig out my notes and begin serious data analysis. Invariably I think that this should be about one week’s worth of work before the serious writing begins. And I’m always then reminded of what my major advisor told me: when you sit down to write the paper, that’s when you realize what you don’t know, and that’s when the hard work begins.
    This is doubly so when a major prediction is falsified or, as often happens, when the data proves the opposite of my favored hypothesis. Then I go through the stages of grieving: shock, denial, bargaining, and acceptance. Luckily, one thing that does improve with experience is that I spend less time in a daze before getting to the exciting bit: I’ve actually learned something! I am not just confirming my own expectations!
    All of my favorite papers have had a long gestation, half because something really unexpected happened. And they are my favorites *because* they took a long time, *because* they required me to really learn something, often by unlearning something else.

  9. Two comments immediately came to mind when I read the post. One was, yes, there are scientists churning out amazing numbers of publications… but to what end? I have sat on numerous interview/ hiring committees and in every instance, when we saw an inordinate number of publications, the first thought was, “Uh oh… one of those.” In most cases that trepidation proved true… that the candidate had churned out oodles of publications placed in low-grade journals, with findings of little significance. Invariably those candidates did not advance through the interview process due to a perception that their time had not been well spent.

    The other thought very much connects to what the author of the post pointed to- i.e., every now & then we come across a result that is counter-intuitive. Understanding these kinds of outcomes if often very difficult, and requires mental gymnastics of years, not months. I encountered such a result in 2010, and it was not until quite recently I was able to explain it, and then publish it.

    I prefer a different phrasing of the phenom than “slow science”… one of “adequate science”. I believe it is always best to ignore the pressures of the outside world and simply focus on generating great publications. Put the pressure on your intellect, not the clock!

  10. I think it’s interesting that the slow science manifesto starts with: “We are scientists. We don’t blog. We don’t twitter. We take our time.” Why are blogging and tweeting counter to doing slow science? I feel like blogging helps me reflect on what I am doing and work through things, which seem in line with their goals.

    • My TREE opinion piece on the IDH grew out of my blog posts over a period of a couple of years. Definitely an example of slow science. It’s only by thinking out loud (as it were) over an extended period of time that I decided that the topic was even worth writing a paper about. It’s also how I figured out exactly what to say and how to say it.

      The folks who wrote the manifesto (which I confess I haven’t read) perhaps aren’t familiar with the range of ways in which scientists use blogs and twitter. Blogs and twitters certainly can be, and are, used in ways that are antithetical to slow science. But any tool can be used badly.

  11. Thank you Brian. That was very encouraging.
    I sometimes felt (and was told so) that I was too slow in publishing my work. But as you say there might be no such thing as being ‘too slow’.

    In my experience it is particularly the theoretical work that requires a lot of time, because the ways how you could specify your model are almost unlimited and you need arguments, assumptions, parameters to tell a consistent and convincing story. And you will go back to the start many times and re-run your simulations (something that is unlikely to happen for a three month field experiment). This can go on for months and can lead into completely useless spirals of hypothesis formation and rejection, if you do not take your time, step back from the details and look at the whole thing to make sure it is still well founded and makes sense.

    • I could not agree more. Theoretical work is daunting… especially if it is novel & there are no publications providing a foundation to build upon. I have found I require two-, maybe three-month breaks after running a group of analyses for a particular hypothesis related to a novel theory. I refuse to look at the files or even think about the work during the interim. Then, when I feel my mind has become unclogged of all the clutter, I go back and look at that 5 to 6 months of work, with a completely open mind. Invariably I ditch anywhere from 50 to 80% of what I did, and use the remainder to guide me to the next batch of ideas & analyses. This regimen has worked really very well for me, and I know my downfalls earlier in my career were often a consequence of not knowing when it was time to put on the brakes. That leads to burn-out, frustration & eventually loss of the desire to pursue it further.

      I am really very very curious how other theoretical ecologists approach things, because I am always looking for insights on how I can better manage & apply my intellectual abilities. So anyone having success with their “schtick”- by all means- please advise!!!

  12. Really nice post which made me think of the recently rediscovered essay “On creativity” by Isaac Asimov, in that novel and big ideas require time, the right circumstances, and they cannot be easily controlled.

    “The history of human thought would make it seem that there is difficulty in thinking of an idea even when all the facts are on the table. Making the cross-connection requires a certain daring. It must, for any cross-connection that does not require daring is performed at once by many and develops not as a “new idea,” but as a mere “corollary of an old idea.”

    It is only afterward that a new idea seems reasonable. To begin with, it usually seems unreasonable. It seems the height of unreason to suppose the earth was round instead of flat, or that it moved instead of the sun, or that objects required a force to stop them when in motion, instead of a force to keep them moving, and so on.”

    The essay also contains some nice ideas on how to create a good environment for group creativity.

    • I essentially spent my career moving from one project to another, across a very broad array of science (from nuclear organelles to biomes); and all along the way, I cultivated my own ideas- as well as those I was paid to develop. None of us are obliged to share those independent pursuits with others, and certainly I never did. But when I knew it was time to “deploy,” I had what I needed to be successful… and those tools were provided by all those PIs paying me to develop their ideas. So, to answer your question- it requires careful planning. Pick & choose what is right for you- not the PI employing you. Use every opportunity to your advantage… and that advantage should go well beyond the standard CV fillers & references for future gigs. In other words, your work as a true scientists does not begin when you land that first tenure track position. It begins when you decide you will dedicate yourself to developing your own ideas, period. And believe you me- there are plenty of tenured faculty who have never gotten to that stage.

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  15. One other way in which ecology can (and should) be a slow science is with regard to long-term data sets. All ecologists who collect data should, as soon as feasible, begin surveys/observations that are repeated at regular (annual or more frequent) intervals. And keep them going for as long as possible, putting off publishing until it’s really telling you something.

    We talk a lot about environmental change and ecological fluctuations, but there are still too few good long (or even medium) term data sets with which to explore patterns and processes.

    I have several such sets of observations and I wish I had started more. Some of them are associated with our undergraduate field course in Tenerife. Annual field courses are a great opportunity to re-survey each year, and anyone running a field course should consider doing it.

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