Posted by: Jeremy Fox | March 16, 2012

Why do fundamental research in a world with pressing applied problems? (UPDATED)

I do fundamental research. I don’t choose what questions to address, what system to work in, or any other aspect of my research based on consideration of ‘societal needs’. I’m not trying to achieve any policy goals, except those of ‘doing good science’ and ‘training good scientists’. Nothing I’ve ever done has any direct or obvious ‘applications’ (I’ve joked more than once that ‘no whales have ever been saved’ by my research). I simply work on whatever question I think is interesting. Hopefully that doesn’t just mean ‘of interest only to me personally’, but nor does it necessarily mean ‘of interest to lots of other people’, be they my scientific colleagues, policymakers, or my fellow citizens. (UPDATE: I emphasize that I do think fundamental researchers ought to be able to explain to others why their work is interesting and important–it’s just that I don’t think those explanations include ‘my work addresses a societal need’ or ‘my work is interesting/important simply because lots of people think it’s interesting/important’).

So why is fundamental research worthwhile? Why should a government agency give me, or anyone, a grant to do it? Especially in a world with pressing practical problems, ecological and otherwise: billions of people are desperately poor, the climate is changing rapidly, species are going extinct at historically-high rates, and money to address these problems is scarce due to the biggest global economic crisis since the Great Depression.

Those are good questions. They deserve good answers. And the answers aren’t obvious. Indeed, one possible answer is that fundamental research isn’t worthwhile, that science for its own sake is a luxury we can’t afford. Even many scientists and champions of science question the value of fundamental research. For instance, Daniel Sarewitz recently argued in Nature that the US government is starving the budgets of ‘mission-driven’ science agencies that actually respond to the ‘public good’, and that the ‘blue-sky bias’ favoring NIH and NSF needs to be ‘brought down to earth’.* In 2007, the UK’s Natural Environment Research Council, the main UK government agency supporting fundamental research in ecology and related fields, decided to focus future funding on seven ‘themes’, all of which are directly related to pressing global environmental problems. Closer to home, the most active Oikos Blog commenter, Jim Bouldin, has argued passionately that much ecological research effort should be reoriented towards directly addressing global environmental problems, particularly climate change. UPDATE: This isn’t a good summary of Jim’s views; see the comments.

And the question of justifying fundamental research won’t go away once the global economy recovers. Opportunity costs are ever-present. A dollar given to me to grow bugs in jars is always going to be a dollar not spent on something else. Plus, the world is always going to have pressing problems that need solving. The second US President, John Adams, famously wrote that he had to study politics and war, that his sons could have liberty to study mathematics and philosophy, so that their children could study painting, poetry, and music. It’s been over 200 years since Adams wrote that, and while I do think we’re closer to the point where everyone can feel free to study painting, poetry, and music–or do fundamental research–without having to justify it, that day is still a long ways off. So if you want to argue for fundamental research, you have to argue that it’s not a luxury good, something we can only afford to spend money on once more pressing needs have been addressed.

What follows represents my best shot at defending my life. I’m not sure how convincing it will be to anyone not already convinced. It’s not a full-on cost-benefit analysis or anything like that (although in my own defense, I’m not sure that even the best economists working on science policy would dare to attempt something like that). It’s just reasons backed up with anecdotal examples, and I’m sure anyone who disagreed with me could come up with their own anecdotes. But if I ever had to justify myself to someone I met at a dinner party or something, these are the sorts of things I’d say.

What follows is also pretty light on links to the massive literature on justifying fundamental research. That’s deliberate. This may sound strange, but this is a sufficiently important issue that I felt like I ought to be able to come up with my own answer, rather than just looking up and quoting the answers of others. For what it’s worth, here’s one randomly-googled article that seems to cover many aspects of the issue.

First of all, I don’t think fundamental research is like John Adams’ art, poetry, and music. I don’t think we fund fundamental research (or not) primarily for the same reason we fund the arts (or not). In my view, the reasons for funding fundamental research actually do have to do with solving pressing applied problems. It’s just that fundamental research helps to solve those problems in non-obvious (but very real) ways.

Second, while there is evidence that the economic ‘return on investment’ in scientific research is positive, those estimates need to be taken with a large grain of salt. Further, AFAIK they don’t do a great job of separating out the ROI on ‘fundamental’ vs. ‘applied’ research, and so they don’t explain why we should fund one type of research vs. the other.

Third, while one good reason to fund fundamental research is that the public actually does want it, I don’t think that’s the only reason or even the strongest reason. It’s true that the public is fascinated by a lot of fundamental science, with expensive physics and astronomy instruments like the Mars Rover, the Hubble telescope, and the Large Hadron Collider being perhaps the most obvious examples. In ecology, think of the popularity of nature documentaries. But the trouble with this argument is that it implies that we should only fund those lines of fundamental research that the public likes (e.g., research on ‘charismatic megafauna’). And while there’s lots of fundamental science that many members of the public probably would find fascinating if they knew about it and if it were pitched to them in the right way, I don’t think fundamental research should be a popularity contest. I say that not because I’m an anti-democratic elitist, but because I think there are good reasons to fund fundamental research that are independent of public interest in that research. Such as:

Fundamental research is where a lot of our methodological advances come from. For instance, rapid advances over the last 10-15 years in fitting mechanistic models to time series data, which are useful for things like predicting future pest outbreaks, have come from fundamental work in population ecology (see here for discussion).

Fundamental research provides generally-applicable insights. For instance, the extinction risk criteria used to produce the IUCN Red List of threatened and endangered species are based in large part on fundamental, generally-applicable models of stochastic population dynamics developed by Russ Lande (Mace et al. 2008). Mace et al. (2008) discuss at length the reasons for this, which are not limited to lack of species-specific knowledge. But it is true that, if you lack detailed, system-specific knowledge, you do want general, broadly-applicable insights to be able to fall back on.

Current applied research often relies on past fundamental research. Isaac Newton wasn’t trying to help put satellites in orbit or a man on the moon when he developed his laws of motion, but NASA engineers rely on those laws. Mathematician G. H. Hardy proclaimed that “pure” mathematics, and especially his own field of number theory, was “useless”, which Hardy considered a virtue because that meant that number theory could never be applied to any “warlike purpose”. But it turns out that number theory is central to public key cryptography, and Hardy’s other example of useless mathematics–Einsten’s equations of relativity–was key to the development of nuclear weapons. And it’s not just fundamental physics and mathematics that turns out to be highly applicable down the road. Genetic algorithms, a routine way to solve practical optimization problems, ultimately derive from Darwin’s theory of evolution by natural selection. It would be trivially easy to keep citing examples here, but you get the point. And no, I don’t think you can argue that we already have all the fundamental knowledge we’re ever likely to need, so that while funding fundamental research was worthwhile in the past, it no longer is.

UPDATE: Here is a short-but-interesting list of the surprising fundamental science behind some well-known research applications (black hole research gave us wifi?!)

Fundamental research often is relevant to the solution of many different problems, but in diffuse and indirect ways. But because those ways are diffuse and indirect, I’m having trouble coming up with a clear-cut example off the top of my head… ;-)

Fundamental research lets us address newly-relevant issues. Societal needs change. So the ‘relevance’ of different lines of research changes over time, often quite fast, and almost always unpredictably. Think of the discovery of the Antarctic ozone hole, emergence of new diseases, and even global warming (I’m old enough to remember a time when global warming wasn’t on anyone’s radar). For that reason, specialists who have only been trained to think about questions of current applied relevance often are poorly-prepared to deal with newly-relevant questions. And it is often impractical at best to rapidly shift training and hiring procedures in an attempt to tightly ‘track’ changing societal priorities. For instance, the practical expertise of government veterinarians failed to prevent the 2001 foot and mouth disease outbreak from quickly raging out of control in Britain. For advice, the British government turned to people like Roy Anderson and Matt Keeling, with fundamental training in mathematical epidemiology. Fundamental researchers, at least the good ones, are broad thinkers with skill sets that let them think intelligently about and address a wide range of problems, so that the way to respond rapidly to a newly-emerging societal problem is to have fundamental researchers who can turn their attention to that problem.

Fundamental research alerts us to relevant questions and possibilities we didn’t recognize as relevant.One function of fundamental research is to discover and evaluate the relevance of previously-unrecognized questions we didn’t even know we needed to ask. Researchers exclusively focused on addressing questions posed to them by policymakers are not well placed to recognize, or argue, that we are asking the wrong questions or trying to solve the wrong problems.

For instance, assessment of ‘instream flow needs’ (basically, how much water can we extract from rivers and streams for human uses while preserving the stream ecology) traditionally has been treated as an engineering question. My colleagues Ed McCauley, Lee Jackson, John Post, and others have argued that this amounts to a poor framing of the problem. A better starting point for thinking about instream flow needs is fundamental knowledge of density-dependent population dynamics in advection-diffusion environments.

As another example, consider alternate stable states and hysteresis, which severely complicate management and restoration since they prevent an ecological system from being easily manipulated into a desired state. The concepts of alternate stable states and hysteresis were originally discovered in dynamical systems theory. Would ‘applied’ ecologists focused on solving system-specific problems ever have discovered these ideas, which are highly relevant to management problems as diverse as lake eutrophication and the collapse of the North Atlantic cod fishery? The possibility of chaos, first widely recognized due to the work of fundamental theoretical ecologist Robert May (1976), is a third example. The fact that chaotic dynamics have proven difficult to demonstrate in nature doesn’t undermine their importance as a possibility that ought to be considered. If you think you might be managing a system that’s inherently unpredictable, you manage it differently (perhaps adaptively).

Fundamental research suggests novel solutions to practical problems. This is related to the previous point. Research directed towards solving particular practical problems tends to focus on a narrow range of solutions to those problems, and a narrow range of obstacles that might prevent those proposed solutions from working. Supposedly ‘relevant’ research often is quite narrowly focused and fails to recognize useful linkages, analogies, and ideas drawn from other fields.

For instance, fundamental research on biodiversity and ecosystem function suggests a novel approach to biofuel production that doesn’t compete with food production or require heavy fertilizer use: sow diverse mixtures of grasses on land that can’t be used for crop production (Tilman et al. 2006).

As a second example, algal biofuel production is plagued by the problem of zooplankton contamination. You don’t get much algal biofuel if Daphnia are eating your algae. The engineers and biochemists who work on algal biofuels have tried all kinds of (often expensive) ways dealing with this. But they never tried the first thing that would occur to any ecologist with some fundamental training in how food webs work: add some fish to eat the zooplankton. Ace fundamental ecologist Val Smith tried this, and as he reported at the last ESA meeting, it works. My buddy Jon Shurin also is taking fundamental ideas from community ecology and showing how they’re very relevant to algal biofuel production.

As a third example, writing recently in Nature, Varmus and Harlow report that US National Cancer Institute and NIH are going to be devoting significant funding to addressing ‘provocative questions’ about cancer. One of which is the recognition that cancer cells are an evolving population and that trying to kill them with drugs selects for drug resistance. Which is something people doing fundamental work in evolutionary biology recognized years ago (Frank 2007, Pepper et al. 2009). Indeed, there are many areas of medicine that would benefit from paying more attention to fundamental ideas from evolutionary biology. Consider in particular the scary possibility that pretty much all the conventional wisdom on how to prevent evolution of drug resistance in malaria, developed by very practical malaria specialists who have largely ignored basic evolutionary ideas, is not just wrong but actually the opposite of right (Read et al. 2009).

Finally, as Dave Tilman’s young daughter showed, you can even use fundamental ideas about resource competition to keep your lawn free of dandelions. Which is probably not the first thing that would occur to someone trained in applied weed management.

The only way to train fundamental researchers is to fund fundamental research. Even fundamental research projects that don’t themselves contribute, directly or indirectly, to the solution of any particular societal problem, now or in the future, contribute by training new fundamental researchers.

So what do you think? Have I justified my existence?

*Note that ecologists are used to thinking of NIH as itself a ‘mission-driven’ agency focused on treating diseases, especially cancer and HIV. Apparently the distinction between ‘fundamental’ vs. ‘applied’ research can sometimes, like beauty, be in the eye of the beholder. But I do think the distinction is reasonably clear, and lots of folks agree with me on that. So while we can quibble about whether some specific bit of research is ‘fundamental’ or not, if you want to argue that this whole post is moot because there’s no difference between ‘fundamental’ and ‘applied’ research I think you’ve got an uphill battle.

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Responses

  1. Given the many values that fundamental research can offer when applied towards the problems we face, I can’t help but feel that we need greater communication between applied and fundamental ecologists. All the tools in the world won’t do any good if the people that can use those tools and implement strategies based upon them aren’t aware of their existence.

  2. *claps*

    • *bows*

    • Hopefully nobody writes *boos* or *throws rotten vegetables* or *walks out* ;-)

  3. I find that the focus not only on applied research but on human-oriented information is one of the great problems with biology textbooks for non-science students. Students actually really enjoy learning about non-human systems and, if I can model making the links for them, learning about basic processes. But the books don’t present either this, or the process of science in coherent fashion, leading to increasing misunderstandings of what science is and the importance of basic research.

  4. I hope to get some time to respond at length but for now I just want to clarify that I do not think that ecological research should largely be oriented around global environmental problems, and most certainly not mainly around climate change issues. I see too much climate change bandwagoning as it is, and have said so on this blog.

    There’s absolutely no question that fundamental–that is to say generalized– research is vital. That’s a slam dunk. The issue, in my mind, is not primarily one of a tradeoff of fundamental vs applied research. The issue is one of a serious lack of a well developed and coordinated research program that integrates fundamental and applied research in a very well thought out and strategic way. But that strategy has to stem from **some** type of underlying philosophy and I argue that such a philosoply, without question, has to be driven by decisions about what’s societally relevant and important. Note that I avoided using the word “planned” because as soon as you use that word, you’re branded as a communist of some sort.

    • Thanks Jim, sorry for not correctly summarizing your views, I’ll correct the post.

      • Not a problem Jeremy, I might not have been as clear as I could have been in the past.

  5. Unfortunately, the answer to your last question is “No…you haven’t justified your existence”. Oh well.

    I much enjoyed your essay, nevertheless. You’ve framed the question and outlined the categories of answers to why basic research is important so very clearly. Congrats!

    You are preaching a bit to the choir, though. I am very convinced by your arguments, but non-scientists are less likely to be. What arguments and examples are most likely to persuade the persuadable lay person? Many of your examples are very convincing to me, but they are mostly ecological arguments, and therefore will not be as compelling to many in the public. Let’s face it, most people are more motivated by arguments framed in terms of economics or health.

    We need more and more diverse examples of the unpredictable nature of practical applications of science. Maybe we can canvass scientists for these kinds of examples, and put them on a web site?

    Regards, Jack Werren

    • Thank you Jack. Re: the diversity of examples, it’s an ecology blog and so I deliberately focused on ecological examples. Plus, many of the most famous examples of fundamental research with unanticipated ‘payoffs’ are from the physical sciences. I didn’t want to repeat those examples.

  6. Jeremy,

    Thanks for your essay on fundamental research – must say I have asked myself the same questions many times. I think the arguments are worth making. But I fear you have answered your own question in the first few lines – ‘I want to do it (my way)’ -> ‘How can I get paid for it?’. In the sense that you normally get paid for doing something for someone else, not for yourself. That doesn’t mean you shouldn’t try, but I have always thought that if you can explain exactly what you want to do (in a grant application for instance) – its not really fundamental research – in my book it might not even be research! So most scientists apply for grants and hope to leave a little headroom for random walks.

    Also Ian Stewart said…’Pioneers must hack their jungles alone, otherwise science would spend all its time sponsoring half baked crackpots.’ (in Does God Play Dice…). I must admit I agree with him, although I’m sure I have strayed into the crack pot area myself a few times. So anyhow, I wish you best of luck – I was wandering around looking for a copy of Oikos 15 (from 1964) and stumbled on this blog – so I better get on with my search for illumination.

    Jay Willis

    • I should clarify that I do think there are reasons why one would choose to address one fundamental research question rather than another. For instance, I list some bad reasons for choosing one’s question here. That is, I don’t think ‘fundamental research’ amounts to doing ‘whatever happens to interest me personally’. I absolutely think any fundamental researcher should be able to make the case for why their work is interesting and important. It’s just that fundamental work is not interesting or important because it directly addresses a specific societal need, or because lots of people happen to think it’s interesting or important (science isn’t a popularity contest). So I do disagree with you, at least a bit–I do think fundamental researchers ought to be able to explain what they want to do and why they want to do it.

      • I agree with that bit about popularity – I do think peer reviews are often about status and so on – they should be done double blind. But perhaps I didn’t explain myself. I have found that when I have done something which is perhaps fundamental research it has involved a chance similarity, or a connection I have made between one field and another. For instance I had an idea about krill and whales from some earlier work I had done on forestry in lowland Europe. So it is difficult to say to a grant authority that I am going to consider problem A, then just spin it around my mind for anywhere up to 20 years, and maybe something that I happen to be working on in the future will spark a connection – which leads to some kind of fundamental insight into problem A… or some other as yet unknown problem.

        I’ll give you another example. I was in an interview with a Research Unit, they had some data languishing on their disk. They wanted somebody to come along and publish the data in some innovative new research. One of the people asked how wide one should go in a research process. I fumbled an answer, but afterward, in that way that you always think of a great answer long after the moment has passed. I thought, how wide? How wide? What answer would you have got if you asked that question of Leonardo da Vinci, or Darwin, Fermi, Maxwell, or Feynman? How wide? Think of the widest you have ever gone, and never go narrower than that in the future. I didn’t get the job :) (By the way I don’t reckon I’m similar to those guys, but if I go running I might as well try to emulate Usain Bolt’s style, even if I would never be half as fast)

        But that is the point I guess, in my view fundamental breakthroughs are about aggregating concepts, bringing together things that have never been combined before. So how can you get somebody to pay for you to wander around in the sum total of human knowledge just in case you stumble on a connection between two things that have never been connected before. I think you’ve got to do it on your own. Sorry :) I see a career in science as a chance to refine you technical capability so that when you discover something interesting you can at least determine if it is new and explain it in a way that recognises earlier work.

  7. Amazing commentary Jay. I agree with you.
    Discovering amazing things but never them placing them in a framework of use for others is of limited value. Every person does not always have to sort out how it can be used but to imagine it once in while is certainly practical.

  8. Have you heard the CD player example? The applied goal (making the CD player) was only possible because of all the basic research that had already been done (http://www.math.mun.ca/~edgar/moody.html) I thought it was cool!

    • No, I hadn’t heard this particular example. Such examples are easy to come by, especially if you’re prepared (as you should be) to trace back a ways, as in my “space flight depends on Newton’s laws” example.

      Which isn’t to say we shouldn’t keep publicizing such examples. Indeed, sometimes I wonder if just the sheer weight of enough such examples would convince doubters, by effectively showing that *all* applied research is really just the fruits of fundamental research.

      We also need more such examples that don’t have to do with physics, computer science, and math.

  9. […] if they do, they remain unconvinced by my arguments for the value of fundamental research. Share this:FacebookTwitterLike this:LikeBe the first to like this […]

  10. […] Fox over at the Oikos Blog has written an excellent piece explaining why fundamental, basic science, research is worth investing in, even when time and resources are limited. His central points […]

  11. […] science for science’s sake In my post on justifying fundamental research, I didn’t argue for fundamental research just for its own sake. Not because I don’t buy […]

  12. […] of their science? For instance, are conservation or other applied projects an easier sell than fundamental research? Can you crowdfund theoretical work? Conversely, how easy is it to crowdfund the scientific […]

  13. […] should look like: I mostly work in a lab, don’t even own any boots to get muddy, and work on fundamental topics that aren’t easily appreciated by the general public. I’m not massively productive or widely cited. But I do things my own way (I have a pretty […]

  14. […] benefit to society or a practical application. This is the so-called fundamental research, the value of which is wonderfully described and argued for over at Oikos Blog. The benefits of fundamental (as opposed to applied) research are often […]

  15. saw this blog recently. But the obvioud answer to the question or issue this article raises is this:

    Fundamental research often gets applied later on. When Einstein was working on his theory he wasnt concerned about the practial applicatons, he was just working towards a theory. But the decades since then have actually proves that his theories can be applied in many ways. So, what is perceived to be fundamental or “useless for society” now, can actually be the most applied later on.

  16. It’s clear why fundamental science is utterly important. You do not need an essay for that. All technology and health care practice (among others) is firmly and directly based on the fundamental science. Period.

    I, however, comment that, as interetesting as it looks like, it’s no longer an easy practice as it used to be. It getting increasingly difficult to do fundamental science …

  17. I really appreciate that people are thinking about problems like these! This was a great article and a great followup discussion. Before continuing with a point of my own, I must point out the interesting irony that Dr. Fox believes that research is *not* like John Adam’s art, poetry, and music for the presented arguments, but *is* like Robert Wilson’s society of good painters, sculptors, and poets if we try to justify research as being good for its own sake.

    I must note that all of the arguments (aside from research being done for its own sake) are based upon the premise that even if fundamental research cannot be immediately used, some component of its architecture may find some use in certain situations or on a future date. It’s extremely relevant to realize that people who engage in this argument and choose to truly do it justice, as Dr. Fox did, still choose to talk about the application and benefit of the research in a positive light.

    However, even with all of this talk about how basic research can be a positive influence on society, consider the example that was brought up previously by Hardy the mathematician, where he was particularly pleased that his research had no practical application (or so he thought). Further, while Hardy failed at providing research with no application, how many others could succeed in such a stubborn endeavor? Many researchers grudgingly and depressingly accept that their research will amount to nothing but a pile of papers that will be forgotten in time, while others maintain the illusion that they will be the select few that will have their research picked up and used by people who will make it all worthwhile, and others mirror Hardy to maintain the fevered anti-corporate struggle to exclude any possibility of their research being anything less than completely ‘pure’ and untouched by profit.

    I therefore cite the attitudes of basic researchers as being a strangling bottleneck for basic research doing good in the world. Instead of optimistically talking about ‘how much good could potentially be done with all of this basic research?’, I find it much more telling to ponder ‘how much good could be done with all of this basic research if people actually wanted to do good?’ I would further argue that many of the success stories from basic research come from researchers breaking the meme and trying to get a spurious applicable idea into circulation. For the small percentage of students who become entrepreneurs, thank you!


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