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

Submitted by drupaladmin on 16 March 2012.

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.

New ideas