Originality is over-rated. (Including by me.)

Image: Tulips, Vera Kratochvil CC-0 released to public domain.

Last week I reviewed a grant proposal for one of the European national granting agencies.  It was an interesting piece of work, which – if funded – would gather probably our best dataset so far to test some longstanding questions in my field.  It was ambitious, thorough, and well planned.  But it didn’t blaze any particularly new path: the techniques were standard, the questions have been in the literature for decades, and every planned analysis has been done before (albeit with smaller and less suitable datasets).

Before I’d even quite noticed, I found that I’d written a sentence in my review saying “There’s nothing original about the proposed research”.  But as I looked at that sentence – and as it glared back at me from the screen – I felt like it was judging me more than the applicant.  And it should have.

You see, originality in science is highly over-rated.  Granting agencies make a big deal about it, often to the extent of asking referees to score it explicitly.  Journals make a big deal about it too – some even flat-out refuse to consider “replication” studies that deliberately seek to confirm or refute an earlier finding:

But this is wrongheaded.  It’s true, of course, that the mission of science is to learn new things about Nature, and doing so requires that we do original work.  But it doesn’t require us to do only original work.

In fact, if we all did only original work, science wouldn’t progress well at all.  A science consisting only of original work would be a science built paper-thin and, therefore, paper-weak.  Our literature isn’t a big pile of facts – by which I mean that the first study to test a hypothesis or use a new technique should never be thought of as settling the question; the first study is something to build on top of, not to build out from.  That’s because any single study may be wrong.  That isn’t a bad thing about science; it’s just the way it is, when we do science in a complex and variable universe.  A single study can be a false positive (or negative), can be a file-drawer-publication-bias artifact, or can be real but be conditioned by too many hidden moderators to generalize*.  If we build understanding out from one result, we may start from false assumptions – leading to studies that don’t even make enough sense to be wrong.  Real progress in science is made not with one-of-everything originality but with the consilience of many studies that, together, suggest a common answer to an underlying question**.  This requires that we do unoriginal science at least much of the time.

Of course, if we need to do unoriginal science, then we need to publish unoriginal science, and we need to fund unoriginal science. And yet I wrote that offending sentence (“There’s nothing original about the proposed research”), because – well, as near as I can figure, because the supposed virtue of originality spends so much time on our lips and in our ears that it’s hard not to let it settle in our brains.  I wrote that sentence despite believing it shouldn’t matter.

Everything comes in threes, right?  The very next day after I wrote the offending sentence, a friend came to my office, upset that a newly published paper “scooped” the Great New Idea he was working on.  That smarts, there’s no denying it – but the mere fact that he used the word “scooped” made clear he’d drunk the originality Koolaid.  That’s two.  And three?  About a paragraph into writing this post, I realized that it isn’t very original either.  And on those grounds I nearly quit.  Wouldn’t that have been ironic?

© Stephen Heard  November 16, 2017

*^Although see this recent Data Colada post for some evidence that at least in psychology, hidden moderators may be less of a big deal than previous meta-analyses had suggested.

**^Not necessarily many identical studies.  The need for exact replications, I think, is greatly exaggerated.  Rather, we want slightly different datasets, slightly different systems, slightly different methods, slightly different takes on the same underlying question.  That’s where robustness comes from.


4 thoughts on “Originality is over-rated. (Including by me.)

  1. Peter Apps

    What you say is true – up to a point. Sometimes one study does settle a point – it falsifies a particular hypothesis once and for all and does not need repeating (such clean results are bound to be way for common in chemistry and physics than in biology of course). Also, there comes a time in any field where enough work has been done to say that our understanding is good enough and we really don’t need to invest resources in answering minor variants of the same question – for example it make no sense to measure yet again the difference in biodiversity between opposite sides of a fence that separates a national park from overgrazed rangeland. The two kinds of unoriginal work that are hugely valuable are the incremental long-term studies of the Whytham Woods type (which I suppose you could argue is just one big original project that has gone on for a long time) and big, well-resourced, meticulously planned and executed work using validated methods that provide a solid anchor / foundation / jumping off point for subsequent work.

    My experience has been that although funders say they want originality, they are unwilling to accept the risks that go with it, and so we get more of the safe and predictable same or at best tiny incremental advances.

    Liked by 2 people

  2. devinbloom

    It seems to me the thing funding agencies and journals are really getting at is: how much will this work advance the field? The attachment to originality is based on the premise that original work will move the field proportionally more than replication. But, as you nicely articulate, that is not always the case! In fact, I’d argue that replication studies that reject previous things we thought we “knew” are even more important than the original work.

    Liked by 2 people

  3. sleather2012

    Interesting – yes we need ‘repeat’ studies – look at the number of papers that incrementally added to the original Southwood & Kennedy idea of trees and plants as islands; I published three myself just adding tweaks and many others added added confirmatory studies. I thought hard about your grant review point as had just done the same thing, but in this case I think justifiably as the proposed work would not have advanced the field substantially if at all.

    Liked by 1 person

  4. Pingback: Arguing with myself | Scientist Sees Squirrel

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