Is basic vs applied research a single dimension?

Jeremy had a post on Monday musing on a propensity for researchers that start out doing basic research and end up mixing applied research in later in their careers. I think the core observation is, on average of course, not by individual, correct. And there were a lot of spirited explanations of why this is in the comments. His framing of a single trade-off dimension between basic and applied is extremely common, and embedded in the funding of many nations’s scientific agencies (e.g. in the US, NSF only funds basic research while the US Department of Agriculture funds applied research).

But I’ve always found that trade-off limiting. Among other things, it implies something cannot be both basic and applied, something which I reject (and Don S gave a pretty spirited rebuttal of in the comments as well). I have found the notion of two trade-off axes put forth by Donald Stokes, in his book Pasteur’s Quadrant: Basic Science and Technological Innovation to be a more useful framing (also see a decent summary of the book in Wikipedia).

Stoke’s two dimensions are:

  • Quest for fundamental understanding – in ecology we would probably call this mechanism-related research.
  • Considerations of use – is the research question chosen with awareness of its usefulness to society?

This leads to a 2×2 table with four quadrants (of which one quadrant is not populated, giving 3 types of research):

Stoke's 2 dimensions of research

As you can see the research that has no consideration for use and no quest for fundamental understanding is considered uninteresting (and presumably nobody would fund it). The other three quadrants though are all valued, as evidenced by the famous scientists occupying them. This is not about whose research is most important.

  • Bohr’s work on the basics of quantum mechanics and the structure of the atom is an example of fundamental research not considering use and would be called “basic” research by most (Stokes calls it pure basic research).
  • Edison’s work inventing the lightbulb, the phonograph etc were all cutting edging and making strong use of science, but were not leading to new fundamental understanding (Stokes calls it pure applied research)
  • Pasteur’s work on microbes leading to vaccinations, pasteurization and the germ theory of disease (Stokes calls it use-inspired basic research).

There are problems with this classification to be sure. Some research that is basic (Bohr quadrant) is also fundamental which, by my definition, means it is truly profoundly informative about how the world works and cannot help but have applications by later researchers even if it is not a goal of the original researcher while other basic research (also in Bohr quadrant) is perhaps more puzzle solving and exists primarily in the mind and doesn’t really tell us about the real world and may never lead to applied research (Jim Clark has argued that neutral theory of biodiversity is an example of this given that you never hear conservation biologists invoking neutral theory). I might arguing iterating through the dynamics of a system with 3 predators and one prey, 3 predators and two prey, 3 predators and 3 prey, etc might fall in this category too. Don S makes a nice distinction between basic and fundamental that I think is close to this idea. And I think that difference between fundamental basic research and non-fundamental (or puzzle) basic research matters. Society should fund fundamental research, but I’m not sure it should fund all basic research (although I stipulate it can be hard to tell the difference in advance sometimes). Or maybe this non-fundamental research belongs in the No/No box I called N/A? Maybe we do more of that kind of research than we think?

And use-inspired research covers a pretty broad spectrum from full-blown stakeholder engaged research on institutional boundaries to basic research cloaked in applicability language that is never really going to go past a basic-research-oriented journal. I think the social-institutional context of research (the degree to which stakeholders are involved and work is done in boundary organizations) probably should be a 3rd dimension (interesting question – can pure basic research be done in a stakeholder engaged way? or does this dimension only apply to considerations for use=yes research?)

But despite these shortcomings (no classification system is perfect), I do think moving from one dimension to two dimensions helps us avoid several false dichotomies.

I am curious what types of ecological research scientists see falling into the three quadrants. Remember all quadrants can have bad or insincere research, but good research in any quadrant is valued. So rating research as falling into one of the three quadrants is not a value judgment. So with that caveat, here are some examples of my interpretation:

  • Bohr-quadrant (pure basic) – metacommunities, mechanisms driving species richness such as the latitudinal gradient, species abundance distributions, role of climate in determining distribution of a species
  • Edison quadrant (pure applied) – estimating the population size or the role of temperature on a specific population, determining habitat requirements of a specific species, predicting (or studying how to increase) growth rates of a managed forest, PVA analysis of one species, niche modelling of one or a set of species, classifying species on the IUCN scale (i.e. endangered, threatened, etc)
  • Pasteur (usage inspired) – global change ecology (estimating the impacts of humans on natural populations and ecosystems and understanding how and why these occur), general population biology, general nutrient cycling, Hanski’s very detailed spatially explicit metapopulation models, wildlife disease ecology, understanding extinction dynamics

What do you think? Do you find two dimensions an advance over one? Which quadrant would you put yourself into? Have I got the examples of the 3 quadrants as applied to ecology right?


20 thoughts on “Is basic vs applied research a single dimension?

    • Nice link – it strikes me the Fundamental/Applied/Developmental categories in their Figure 1 are not a bad fit to the Bohr/Pasteur/Edison categories in Stokes’ quadrants.

      I completely agree that the lines are more blurry/shades of grey than the above discussion makes them seem.

  1. It’s an interesting way to frame the question, Brian, but I think that a lot hinges on what is meant by “fundamental understanding”. For example it appears to me that there is a continuum between fundamental understanding that can be applied to ecology as a whole (at one end) and fundamental understanding that can be applied to just a single species or interacting system at the other end. Work at that narrow, N/A end may never be fundable, as you suggest, but it can be extremely valuable if it adds another data point to a future meta analysis, quantitative review or macroecological study. So I think N/A is wrong in this context, this is work that can and should be done.

    • Interesting points. As I wrote this I increasingly wondered about the N/A box. In general I hate that trick (always bothered me about Grime’s triangle too). I guess I was proposing that research that wasn’t fundamental (i.e it is not usage inspire but also not deeply revealing about how nature works) belongs in that N/A box.

      It seems to me you are making a different proposal; that work that is confirming or supportive to later fundamental research might belong in that box.I agree that N/A box is a very Platt-like or physics-like view of the world where there is a single decisive experiment. Multicausality in ecology means we will never be in that world. I do wonder if something is intended to aid future fundamental research if it belongs in the Bohr box or the N/A box.

      More broadly your point raises for me the interesting question of where does long-term monitoring go? It may have applied goals. But can be vital for fundamental work. Look at how much theory has been developed using the BCI data. We’re not the only field like this – the sky surveys in astronomy are probably comparable. Just collecting data is critical to research in ecology (and astronomy) but may not be goal-directed to fit in any specific box.

      • “I do wonder if something is intended to aid future fundamental research if it belongs in the Bohr box or the N/A box.”

        The sort of work I’m thinking of is usually never intended to be anything other than a curiosity-driven piece of research, e.g. “what are the effective pollinators of plant X?” There’s dozens of such studies in the field of pollination ecology and by themselves they don’t add much in the way of “fundamental” work. But collectively they are invaluable for addressing larger-scale questions such as whether tropical plants more specialised in their interactions or more likely to be pollen limited.

        Yes, agreed, long term monitoring is a very good case in point.

      • Your example of specific pollinators seems to me like a good candidate to fill the NA box (perhaps it should be the “natural history” box – a term which I use with respect even if others use it pejoratively)

      • I was waiting for some one to say this 🙂 No, in this case, it’s not “just” natural history. Determining whether or not a particular flower visitor is an effective pollinator requires some quite technically demanding experimental field work, involving bagging flowers and allowing single visits to virgin stigmas, collecting stigmas, staining them and counting pollen tubes, or waiting until seed set has occurred, and counting those. It usually also involves hand pollinations to determine selfing rate and pollen limitation, and observations of pollinator behaviour (distances flown between flowers, for instance). In plants with multiple species of pollinators (which are the majority) this is a lot of work to obtain decent sample sizes that goes far beyond why I would consider to be “natural history”. Yet still I wouldn’t see this as “fundamental” in the way it’s being used here.

      • Glad I didn’t disappoint you! 🙂 I guess we may have different definitions of natural history. It does not only include casual observation to me. I think of AmNats Natural History notes for example. For that matter the Victorian natural historians put a lot of work (albeit much less quantitative and more sweating through the jungle than you are describing) into their work as well. As I say, I know natural history is too frequently used by ecologists as a pejorative term. But I think it is a beautiful term with a lot of wonderful history describing a very valuable (and often intensive) contribution. I guess to me it just is a way of valuing the opposite of generality.

  2. Excellent post, Brian- in fact, I’d say maybe the best I’ve seen here in awhile.

    “Pasteur’s work on microbes leading to vaccinations, pasteurization and the germ theory of disease (Stokes calls it use-inspired basic research).”

    Medicine, at least in the US, transitioned to this model of research in the early 2000s, when they required many NIH funding programs to emphasize the “bench to bedside” approach. In other words, they demanded immediate medicinal therapies arising from basic research. I believe, in large part, this has fueled for example the rapid advances in cancer therapies- i.e., individualized care.

    I have adopted that model into my basic research, and found it very helpful, if not at times annoying as hell… Previously, I did not push myself to seek applied aspects of theoretical work, I suppose assuming someone else would eventually do it for me. But the truth is, unless you have revealed something truly amazing on the theoretical side, it’s unlikely someone else will bother doing that for you.

    Bench to bedside… computer to creekside. I kind of like it, even though it makes life a bit more difficult.

    • I doubt it is a coincidence that the use-inspired box is named after somebody in medicine. And I think you are absolutely right that unless the scientists themselves take some responsibility for pushing things out into the applied world, it is unlikely to happen. Some science policy researchers call this the loading dock problem. We throw a lot of potentially useful research into a journal on the assumption somebody else will pick it up. But it is not so clear that transfer is very frequent or efficient.

  3. A mixed response to yesterday’s and today’s posts and comments…

    The ARF Hypothesis (Applied Requires Fundamental): Most students begin grad studies (and eventual careers) in ecology with some mixture of (1) intense curiosity about how the world works, and (2) a desire to do something useful for humanity. If (1) is dominant, the student tends toward projects that involve mastering the theoretical and conceptual principles underlying a discipline, regardless of whether there is immediate application of their specific results. But once the fundamentals have been mastered, they are in a strong position to apply them effectively, and so they do. If (2) is dominant, I think there is actually a risk of not first mastering fundamental principles, and so doing weaker applied ecology. Not only does it seem that many people have followed the path Jeremy described, but that they are also the leading researchers in applied areas of ecology. Coincidence?

    (Everyone poopooed Jeremy’s hypothesis; it sounds entirely plausible to me.)

    • I don’t know that I agree that the famous basic ecologists who have started doing applied work are the leading researchers in the applied world. They may be best known to us. But there are a heck of a lot of people doing really important work that never took that path. Some of them are in conservation biology and some of them are not in academia at all.

      I also still reject the notion that applied work is somehow more compatible than basic workvwith short attention spans and lack of currency in the reading.

      I don’t disagree that applied-targeted students benefit from training in basic ecology concepts. I just had two agriculture (weed ecology) students in my community class and I think they got a lot out of it. But I don’t think that is asymmetric. I think basic-targeted students would get a lot out of understanding the questions and challenges in the applied world. I know I learned a lot from the two aforementioned students.

      In short, I am going for the BARE hypothesis (Basic and Applied Require Eachother).

      • “In short, I am going for the BARE hypothesis (Basic and Applied Require Eachother).”

        This is the Acronym Police. You are under arrest. You are charged with one count of Smooshing Words tOgether Tomakeanacronym (SWOT). Put down the acronym and step away from the keyboard.

      • Now we need some data to test all the hypotheses! But I’m far too busy and tired to think about how to test a question of such fundamental importance. Or is it of applied importance? If only I was younger… 🙂

      • Well, to BARE myself in this Blog; Or is it beating an ole horse?
        Brian is right [ with BARE], Jeremy having too much fun, and Mark busy pushing the frontiers of community structure, which may/may-not change views about biodiversity/conservation-biology issues.
        I was trained in Fisheries [ 2 degrees] and spent a year in grad school in applied Entomology, looking at how parasitoid wasps control pests. I know zero about funding opportunities now, but the usefulness of GOOD applied research to basic/fundamental ecological questions is BIG. And the reverse; many discussions in parasitoid biology, in applied contexts, begin with my generation’s sex ratio ideas. Or foraging ideas.
        2 other examples: the good people in designing biological control [ read parasitoids and pests] know a lot about how 3 trophic levels work. and meta-analysis of life history data from fisheries has played fundamental roles in life history theory. Likewise basic studies on life history evolution have informed fisheries. I have had great talks with fisheries and biological control folks for over 40 yrs; they clearly talk with me because its useful to them.
        Having said this I also know its hard to get the 2 groups [ simplified] to really talk.

      • I think we (me included) might be mixing up (i) explanations for the observed pattern and (ii) which of basic and applied research require the other more/less. I agree about the mutual basic-applied reinforcement, while also thinking my explanation might help explain how some people end up following the basic-to-applied career trajectory.

  4. Good post. I work on the ecological side of ecosystem services research – perhaps one research field that crosses the dimensions. Sure it’s usage inspired, but identifying the underlying mechanisms between ‘services’ and related biodiversity-ecosystem function relationships is a key challenge that would lead to advances in both basic & applied ecology.
    But I find the basic vs applied ecology argument frustrating. I agree with what I think Jeff is saying above. All ecological research can be ‘applied’, whatever the original goal of the research. So N/A science doesn’t really exist….and delimiting research to these dimensions doesn’t really help ecology as a whole, especially when trying to communicate the importance of ecological interactions to non-scientists.

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