In praise of backwards thinking

What is science? This is a favourite opening gambit of some external examiners in viva voce examinations. PhD students, be warned! Imagine yourself in that position, caught off-guard, expected to produce some pithy epithet that somehow encompasses exactly what it is that we do.

It’s likely that in such a situation most of us would jabber something regarding the standard narrative progression from observation to hypothesis then testing through experimentation. We may even mumble about the need for statistical analysis of data to test whether the outcome differs from a reasonable null hypothesis. This is, after all, the sine qua non of scientific enquiry, and we’re all aware of such pronouncements on the correct way to do science, or at least some garbled approximation of them.* It’s the model followed by multiple textbooks aimed at biology students.

Pause and think about this in a little more depth. How many great advances in ecology, or how many publications on your own CV, have come through that route? Maybe some, and if so then well done, but many people will recognise the following routes:

  • You stumble upon a fantastic data repository. It takes you a little while to work out what to do with it (there must be something…) but eventually an idea springs to mind. It might even be your own data — this paper of mine only came about because I was learning about a new statistical technique and remembered that I still had some old data to play with.
  • In an experiment designed to test something entirely different, you spot a serendipitous pattern that suggests something more interesting. Tossing away your original idea, you analyse the data with another question in mind.
  • After years of monitoring an ecological community, you commence descriptive analyses with the aim of getting something out of it. It takes time to work out what’s going on, but on the basis of this you come up with some retrospective hypotheses as to what might have happened.

Are any of these bad ways to do science, or are they just realistic? Purists may object, but I would say that all of these are perfectly valid and can lead to excellent research. Why is it then that, when writing up our manuscripts, we feel obliged — or are compelled — to contort our work into a fantasy in which we had the prescience to sense the outcome before we even began?

We maintain this stance despite the fact that most major advances in science have not proceeded through this route. We need to recognise that descriptive science is both valid and necessary. Parameter estimation and refinement often has more impact than testing a daring new hypothesis. I for one am entranced by a simple question: over what range do individual forest trees compete with one another? The question is one that can only be answered with an empirical value. To quote a favourite passage from a review:

“Biology is pervaded by the mistaken idea that the formulation of qualitative hypotheses, which can be resolved in a discrete unequivocal way, is the benchmark of incisive scientific thinking. We should embrace the idea that important biological answers truly come in a quantitative form and that parameter estimation from data is as important an activity in biology as it is in the other sciences.”Brookfield (2010)

Picture 212

Over what distance do these Betula ermanii trees in Kamchatka compete with one another? I reckon around three metres but it’s not straightforward to work that out. That’s me on the far left, employing the most high-tech equipment available.

It might appear that I’m creating a straw man of scientific maxims, but I’m basing this rant on tenets I have received from reviewers of manuscripts, grant applications or been given as advice in person. Here are some things I’ve been told repeatedly:

  • Hypotheses should precede data collection. We all know this is nonsense. Take, for example, the global forest plot network established by the Center For Tropical Forest Science (CTFS). When Steve Hubbell and Robin Foster set up the first 50 ha plot on Barro Colorado Island, they did it because they needed data. The plots have led to many discoveries, with new papers coming out continuously. Much the same could be said of other fields, such as genome mapping. It would be absurd to claim that all the hypotheses should have been known at the start. Many people would refine this to say that the hypothesis should precede data analyses (as in most of macroecology) but that’s still not the way that our papers are structured.
  • Observations are not as powerful as experiments. This view is perhaps shifting with the acknowledgement that sophisticated methods of inference can strip patterns from detailed observations. For example, this nice paper using Bayesian analyses of a global dataset of tropical forests to discern the relationship between wood density and tree mortality. Ecologists frequently complain that there isn’t enough funding for long-term or large-scale datasets to be produced; we need to demonstrate that they are just as valuable as experiments, and recognising the importance of post-hoc explanations is an essential part of making this case. Perfect experimental design isn’t the ideal metric of scientific quality either; even weak experiments can yield interesting findings if interpreted appropriately.
  • Every good study should be a hypothesis test. We need to get over this idea. Many of the major questions in ecology are not hypothesis tests.** Over what horizontal scales do plants interact? To my mind the best element of this paper by Nicolas Barbier was that they determined the answer for desert shrubs empirically, by digging them up. If he’d tried to publish using that as the main focus, I doubt it would have made it into a top ecological journal. Yet that was the real, lasting contribution.

Still wondering what to say when the examiner turns to you and asks what science is? My answer would be: whatever gets you to an answer to the question at hand. I recommend reading up on the anarchistic model of science advocated by Paul Feyerabend. That’ll make your examiner pause for thought.

* What I’ve written is definitely a garbled approximation of Popper, but the more specific and doctrinaire one gets, the harder it becomes to achieve any form of consensus. Which is kind of my point.

** I’m not even considering applied ecology, where a practical outcome is in mind from the outset.

EDIT: added the direct quotation from Brookfield (2010) to make my point clearer.


5 thoughts on “In praise of backwards thinking

  1. Pingback: Recommended reads #70 | Small Pond Science

  2. Z.L. 'Kai' Burington

    Every good scientific work does not necessarily need to test hypotheses (in the sense of strong inference) because many hypotheses are tested by reciprocal illumination (i.e., all of natural history research). But every good scientific work should /include/ hypotheses, and represent some sort of progress of thought or observation towards answering these questions.


    1. Markus Eichhorn Post author

      I agree in principle, but depending on your definition of ‘hypothesis’, this might end up as a pretty low bar. Any paper needs to justify to the reader why the work is worth doing, and that means persuading them that there is a fundamental question which it make a contribution towards answering. Whether that has to be a hypothesis in the Popperian sense is a different matter.



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