What, ultimately, are we doing with science? The idealistic view (most likely, I would suggest, to be held by the general public), is that we are discovering ‘the truths of the universe’. If on the other hand you were to ask someone mired in the day-to-day realities of research if this is how they spend their time, you might raise a wry smile.
And what is an individual scientist to do? Particularly for PhDs and early career researchers, the scale of the challenge feels immense: the problems we want to solve are so complex, and the space of possible approaches, techniques and solutions so vast, that how can one possibly discover anything noteworthy except through dumb luck? What is the point?
It is fashionable to emphasise to students that they are not expected to make a big contribution to science; that to start with they will be pushing forwards the bounds of our knowledge by only the tiniest amount – and that’s ok.
But I’m not sure that this is the correct response. I don’t think it’s the correct response because I don’t think we should be telling students at the outset of their career to tone down their ambitions, to look only down at the ground immediately in front of them and never up at the sky. And I also don’t think it’s the correct response because I don’t think many students, particularly if they really are ambitious, will believe it. I certainly didn’t. Instead, I think we need all to agree on a better description of what science is.
Much of my own thinking about this topic has been inspired by the work of the mathematician Bill Thurston, and by Chris Olah and Shaun Carter at the Distill project, on the topic of ‘research debt’. If you’re not familiar with this work then I would highly recommend looking over it – in my view, the idea of research debt should be regarded as one of the most important examples of practical philosophy of science since Popper, and both Thurston, and Olah and Carter naturally explain their work with greater ease and clarity than I can achieve here.
In brief, research debt refers to the cost that accrues at an institutional level of poorly explained ideas. For example, Olah and Carter describe research as being like climbing a huge mountain of literature – then, when you reach the top and start doing your own work, you're adding more rocks on top of the mountain to make it even harder for the next person to climb. The insidious nature of research debt is that it is multiplicative – if 10 people want to understand an idea that at present is unnecessarily complicated and poorly explained, then the cost incurred in terms of those people’s time and human energy is multiplied 10-fold. Conversely, if the author of the idea expended their own time and energy to make it easier to understand then the return on that investment (the cost saved for others) would be magnified 10 times!
Bill Thurston's influence can be summed up even more succinctly. The point of mathematics (for which, read science more generally) is not to “prove theorems”; rather it is “to advance human understanding of mathematics”. (Elsewhere, Thurston also tells a very interesting, personal story on the decay of a whole field of mathematics that struggled under the weight of too much research debt).
In the early days of my PhD, as I grappled with the question asked by all PhD students (and probably lots of more senior researchers too) at some point – why am I doing this? – I spent a lot of time mulling over these ideas of Thurston, Colah and Carter. As appealing as I found this conception of science to be, in all its idealism and humanism, I found it difficult to reconcile with the realities of experimental research. The primary requirement of my job is to conduct experiments and thereby uncover new facts about the world. It is true that in writing this work up and sharing it with the scientific community I need to achieve clarity of expression and understanding, but surely this is not the whole point of the empirical sciences? Perhaps the work of simplifying and distilling down existing ideas is of prime importance only in theoretical subjects like mathematics, where ideas are all that one has.
For a while I toyed with the idea that really we have two jobs to do as scientists: we have to make new discoveries and we have to communicate these to others. Some people might specialise: we all know researchers who are very good at making discoveries and creating new knowledge, but awful at putting this into a form of words that others can understand; conversely there must also be a class of people who are less adept at discovering new information but who are very good at getting to their essence (though I am sure that this second group is less common, and certainly less well rewarded for their contributions).
I realised, however, that this dichotomous view is wrong – the discovery of knowledge and the communication of that knowledge are not different jobs, they are one and the same. In other words, science depends entirely on communication.
What I mean by this is that, for a scientific discovery to merit that term at all, someone else must be able to learn from you whatever fact or information you have uncovered in less time and with less effort that it took you to acquire it. This means that as well as acquiring new information you must have reorganised it in a useful way. Consider the extreme case – you have devoted an entire career (with all the hard work, late nights and sacrifices that entails) to developing a monumental idea – a unified theory of physics, say, or a cure for cancer. If the idea is so complex and so poorly distilled that it would take another whole career for a student to learn it from you then, I would argue, you have not discovered anything at all. Instead, each generation would have to rediscover your theory afresh. You have just collected information, but you don't have anything useful to communicate.
As a thought experiment, imagine a computer which is able to predict the future perfectly, but only by simulating everything about the world in infinite detail. In that case, most people would say that the computer doesn’t have what we would consider knowledge – it hasn’t extracted anything constant or fundamental about the way the world works. In computer terms, knowledge requires compression. Likewise in scientific research, making a discovery requires not just collecting some set of observations for the first time but condensing that information down as well, so that it can be passed on to others.
At its most fundamental then, our entire job as researchers – even when we are working to uncover new knowledge about the world – involves distilling information for others.
Following on from this, I have realised that success as a researcher can be roughly quantified by the ratio between the time (and effort) it took me to understand an idea, and how quickly I can get someone else to understand it. This is the secret of good science and should be paid much more attention than citations, h-index or other spurious measures of quality.
This realisation, I think, leads to better science. We need to place more value on people doing interpretive work – reformulating an existing idea to make it more intuitive, or identifying deep conceptual connections to ideas in other fields, can be just as useful as conducting new experiments or observations. Indeed it can be even more so if you work in a hyperspecialised field that is understood by very few people. I also think this framework fits in to some of the discussion about slow science that others have had previously – fast science, like fast food, is often indigestible and produces results which cannot have as much influence as if the authors had taken more care over reducing, as far as possible, their research debt.
Finally, I hope this way of thinking about research gives some encouragement to any PhD students who, as I did, questioned from time to time whether this difficult job is worth it given the relatively long odds of making a really substantial (i.e. ego-satisfying) discovery. You can do important work – and make a really significant contribution to the world – not by having a huge citation count, being published in Nature or winning a Nobel prize, but by focussing on problems with the biggest ratio between the time you have to put in to work something out versus the time taken to fully communicate your ideas to others.
Addendum 2/10/22
"For these reasons, a young scientist must not be disheartened if he does not become the eponym of a natural principle, phenomenon, or disease. Although the importance of discoveries may be overrated, no young scientist need think that he will gain a reputation or high preferment merely by compiling information – particularly of the kind nobody really wants. But if he makes the world more easily understandable by any means—whether theoretical or experimental—he will earn his colleagues gratitude and respect."
– Sir Peter Medawar, Advice to a Young Scientist