As I described in a previous post, a long-standing topic of discussion is the usefulness of a given scientific endeavor or study. Along these lines, science is often divided into BASIC and APPLIED. Applied science is – by definition – useful. It cures some disease. It improves crop levels. It saves some endangered species. Basic science is – at least classically – not obviously or immediately useful. Instead, it addresses a (hopefully) interesting question – interesting at least to the researcher. Sometimes called “curiosity-driven” science, basic research might one day have great utility but, at the time it is conducted, its uses aren’t obvious.
|The motivation for my earlier post on basic vs. applied science.|
Basic science was once considered an admirable pursuit – perhaps even preferable as an intellectual, university-based enterprise. More recently, however, universities and funding agencies want to hear how your research – whether basic or applied – will have “broader impacts” or “direct benefit to the people of ...” No longer is it enough for the science itself to be interesting and clever and well designed; it also has to have a clear utility. When justifying a research project, these pay-offs are expected to be clearly and forcefully presented, usually at the outset of a proposal and in an explicit section at the end.
For basic scientists in ecology and evolution, these applied justifications tend to involve conservation (e.g., saving some endangered species or place), management (e.g., of natural resources), discovery (e.g., new drugs), or ecosystem services (e.g., greater biodiversity generates greater productivity or resilience or whatever). In many cases, the specific link between the science and the proffered application is PREDICTION. For example, “we need to be able to predict what is going to happen, in the face of environmental change or management actions, if we are going to design effective strategies for conservation or management.” This sort of justification is a natural and easy one because we can always say “If we don’t understand the system well, we can’t predict it. My research will help us to understand the system better, which will improve prediction, which will be useful, right?”
Just last week I – along with 21 other scientists – published an opinion/review paper in Science amplifying this last point. Specifically, we need to predict what will happen with climate change and – to do so accurately – we need much more information about organisms, communities, and ecosystems than we currently have. In this post, I would like to play Devil’s Advocate to my own paper by arguing that prediction is often hopeless.
|From our Science paper.|
A first important distinction is whether we wish to make a prediction or whether we wish to make an ACCURATE prediction. It might seem obvious that we want the latter but even the former is sometimes hard. That is, we might not have enough information about a given system to even speculate effectively as to whether or not some action (e.g., climate change) will have a particular effect on a particular species. Most of the time, however, we are able to make some sort of prediction based on intuition or similar systems or mathematical models or experiments or whatever. So the real concern becomes “how correct (accurate/precise) will be our predictions?”
The accuracy of prediction will depend on the type and precision of prediction. For instance, we might first want to predict simply WHETHER a given environmental change or management action will have an effect at all. Here we might be safe in many instances. Will climate change influence biological diversity? Yes! If the environmental change is large, something will respond to it. However, this isn’t the sort of prediction that we – or the public or managers or governments – care about.
We might next want to predict the DIRECTION of an effect. In some cases, this will work fairly well. For instance, we can safely say – based on many examples from nature – that climate warming will advance the timing of reproduction of many plants and animals and that commercial fisheries will lead to smaller body size in harvested populations. A few exceptions will certainly occur but these will tend to be of the type that “prove the rule.” In many other cases, however, predictions as to the direction of an effect will be incorrect. Will climate warming increase or decrease local biodiversity? Hard to say. Will fish harvesting increase or decrease productivity? It depends. In such cases, increased information – including from “basic science” – might improve predictions.
Experience teaches, however, that expectations developed from theory, from related systems, and from detailed information are – not infrequently – incorrect.
At the most precise level, we might want to predict an effects size, such as a particular rate or endpoint state. How fast will species be lost with climate warming? How many species will be present 25 years from now – and where will they be? How small will harvested fish become and how quickly will they recover when fishing ceases? I suggest that – in many cases – predictions of this sort will be hopelessly inaccurate, except perhaps by blind luck. Each system (and year) has so much contingency that prior information will not be sufficient. Of course, this is precisely the logic that we invoke when seeking funding: “We can’t make accurate predictions unless we get more information, so give me some money to get it.” It is certainly true that if one had complete information on the driving forces in any given system and complete information about how those driving forces will change in the future, then accurate predictions of endpoints and rates might be possible. But this “complete” information is generally unattainable.
|Another opinion in Science about prediction|
In short, many of the arguments one reads in proposals that the particular basic science being proposed is critical for better prediction are really just smoke-and-mirrors or, perhaps more accurately, a bait-and-switch. Five years later: “Although I didn’t make better predictions, I did do some cool stuff anyway, no?” Of course, these studies can also weasel out of accountability by saying “Here is some new information that other people might find useful in making better predictions” or they might say “Here are some new predictions.” – with the last being particularly disingenuous because the accuracy of those predictions won’t be known for sometimes decades.
My point in this post isn’t that basic science should be abandoned in favor of applied science. My point instead is that it would be nice if we could all just drop the applied BS at the start and end of our proposals. That isn’t why we are doing the study – it is just what we think the reviewers want to hear. The reality is that science has made incredible strides in the past few centuries – and most of those advances, I will speculate, were made by basic rather than applied science. Think of all of the ramifications Darwin’s theory or natural selection, and – coincidentally – all of the incredible and amazing applications. At the time, however, Darwin – and the people who read his book – didn’t focus on its potential applications but rather its potential to explain how the world around us came to be.
I had better circle back to that Science paper for which I am here playing Devil’s Advocate. It is certainly true that we don’t have enough information to make good predictions of how biodiversity and species ranges will change with climate change. It is also true that getting more information about those species and environments has the potential to improve predictions – although we won’t know if we are correct for decades. Thus, I am not disputing the main arguments we made in the paper. Instead, I am using it as a jumping-off point to argue that additional information is probably even more useful simply in improving our understanding of the world around us, whether or not we attempt predictions. Sometimes this improved basic understanding will eventually have massive benefits for biodiversity and the humans that depend on it.
I think it cheapens, and potentially slows, progress in science to require it (or encourage it) to have obvious immediate applications. The best route to the best possible future applications is to simply turn researchers loose to study what they feel is most interesting, whether applied or basic. Basic research isn’t flawed and in need of an applied crutch to hold it up.
After I posted this, I was told about a similar post on Dynamic Ecology:
After I posted this, I was told about a similar post on Dynamic Ecology: