What should we do in science? This is a question about pursuitworthiness of research programs. The question concerns which research programs we should develop further, i.e. which programs are worthy of pursuit. Analyses of pursuitworthiness are motivated by the need for an ability to respond to possible future changes and demands. These changes and demands may range from epistemic to those generated by changes in values and preferences. For example, we may face a scientific crisis in which our best theories no longer answer the questions we find interesting. Or we might wish to rethink who chooses which questions are relevant in the first place. Pursuitworthiness is a question about the potential of different research programs. The relevant set of research programs that need to be considered includes both existing research programs with accepted theories and potential research programs that have not (yet) been developed.
However, Shaw (2022, 104) points out that the contents of the criteria of pursuitworthiness are often explicated in terms of accepted theories. It appears that, in one way or another, the assessment of the pursuitworthiness of a research program depends on its relation to accepted theories and the current knowledge-base, i.e. the existing cognitive horizon (see Šešelja & Straßer, 2014 for the notion). In a sense, this is a natural way to assess pursuitworthiness, as we cannot rise above our current knowledge. However, this creates problems for the analysis of pursuitworthiness.
First, following Feyerabend (1993), Shaw notes that, in hindsight, some of the most pursuitworthy research programs, such as Galileo’s, were not consistent with the existing cognitive horizon in any meaningful sense (2022, 105). It seems that every criterion of pursuitworthiness is too restrictive and could potentially cut off valuable research because the criteria require consistency with the existing cognitive horizon. This already questions the notion of pursuitworthiness, but there is an even more serious problem.
Secondly, and more fundamentally, the assessment of pursuitworthiness in terms of the existing cognitive horizon may be self-defeating. As Shaw summarizes,
“[According to Feyerabend,] the very structure of pursuitworthiness judgments is problematic. Since any benchmark within a cognitive horizon used to assess a pursuit can become undermined by the pursuit itself or exogenous changes in a cognitive horizon, then any pursuitworthiness criteria may be self-defeating. The proper cognitive horizon to utilize would be the result of the pursuit, rather than a precondition for it. This entails that we can only determine that research is pursuitworthy in retrospect.” (2022, 105.)
It appears that we can assess the pursuitworthiness of a research project only if we can predict the future of science. Predicting the future of science is impossible because we need to use the existing cognitive horizon to make those predictions while the future can change that very horizon. Because predicting the future of science is impossible, we cannot assess the pursuitworthiness of research programs, the reasoning concludes. In what follows, I will tackle this issue. I will argue that there is much more to the study of possible futures of science than attempting to predict the future of science. I will also argue that the assessment of pursuitworthiness does not depend on our ability to predict the future as long as we can systematically map scenarios of the future. While Shaw (2022) argues that there are contexts where aspects of the future of science can be predicted with some success, the arguments against the possibility of predicting the future of science are strong enough to suggest that we need a general approach to the estimating of the future of science. Such an approach enables us to estimate the future of different aspects of science in many different contexts. Even though it might be an empirical question where and to what extent the future of science can be reliably predicted, the general approach guarantees that we have a way of understanding the future of science in contexts where predictions are neither possible nor our goal (for example, when we wish to prepare for a crisis). The general approach also underlies the assessment of criteria of pursuitworthiness, as we will see in the next sections.
In addition to the argument concerning the potentially self-defeating use of the existing cognitive horizon, there are surprisingly few explicit arguments against the possibility of predicting the future of science. The arguments seem to stem from the same insight: If we were able to predict a scientific discovery or innovation, then we would have already achieved the discovery or innovation This is a contradiction. Therefore, we cannot predict the future of science. There are two slightly different versions of this problem. First, if we were able to describe a radically new conceptual innovation of the future, we would have already made the innovation. “Any invention, any discovery, which consists essentially in the elaboration of a radically new concept cannot be predicted, for a necessary part of the prediction is the present elaboration of the very concept whose discovery or invention was to take place only in the future (MacIntyre, 2007, 93). Given that we may have radical conceptual innovations in the future, it follows that our conceptual schemas are insufficient for predicting the future of science. Secondly, even if we had a sufficient conceptual schema and made a prediction concerning a novel discovery, we would not have sufficient justification for our belief that the discovery will be made. If a theory T implies that some D is the case, and if we do not already believe that D, then we do not have enough justification for T. Once D is discovered, we might believe in T because D justifies it; but at this point, we can no longer predict D. (See Finocchiaro (1973, 37) for a similar argument.)
The unpredictability of science is usually taken for granted in philosophy. It has also been thought that this unpredictability has extremely wide reaching consequences. Here is classical summary by none other than Popper:
The course of human history is strongly influenced by the growth of human knowledge. [However, we] cannot predict, by rational or scientific methods, the future growth of our scientific knowledge. We cannot, therefore, predict the future course of human history.” (1957, ix-x.)
Next, I respond to the considerations above. I will build my response to the issue on three observations. First, the arguments above assume that there will be somewhat radical crises and changes in our scientific knowledge in the future. To see this, notice that, for example, if we assume that our current theories and knowledge-base are rock-solid, then there is no risk of a self-defeating use of them in the assessment of the pursuitworthiness. I will not assess the strengths and weaknesses of the assumption concerning radical changes. However, I wish to point out that it is still an assumption. We can have many other assumptions about science as well. For the very reason that we cannot predict the future, we cannot know which of the assumptions is ultimately true. However, we can systematize different assumptions and provide a map of future scenarios that these different assumptions generate (see the next section). This enables us to become aware of and prepare for different future possibilities. While the whole point of estimating the future of science depends on the view that science may change in the future, it is unclear how much it can change and why. A central aspect of the estimating of possible futures of science is to map how much science can change and for what reasons.
Secondly, the arguments assume that the most important thing to know about the future of science is what, exactly, will be known, i.e., the exact results of science. Even though it would undoubtedly be great if we knew what discoveries and conceptual innovations will be made in the future of science, it does not follow that there are no other important things that we can assert about the future of science. For example, the motivation for expensive experiments with fusion power is not that we are able to predict their outcome (whether or not fusion power will be commercially useful) but that we can estimate that there are good chances that we get to know what we wish to know (i.e., it can be expected that the experiments are good enough to inform us about the possible commercial use of fusion power) (e.g. Claessens, 2020, Ch. 12). Even if we cannot predict the future results of science, we can still assert important things about the future such as that some experiment is good enough to provide a valuable outcome (even if we are not predicting the outcome). The arguments against the possibility of estimating the future of science are therefore seriously limited in their scope when they focus merely on discoveries and innovations.
Thirdly, one crucial element in the arguments is the assumption that the goal of the study of the future is to predict particular events, such as discoveries and innovations. This appears to be a way too restricted stance towards future-oriented thinking. It is questionable, to say the least, in general (i.e., not just with respect to scientific discoveries and innovations), whether the accurate prediction of particular events in human society is the gold standard of successful futures research. Given that the main objectives of futures research are enhancing understanding and challenging conventional thinking, there is much more to futures research than predicting. As we will see in the next sections, enhancing understanding and challenging conventional thinking can be achieved by formulating many different scenarios of the future and the formulation of the scenarios has little to do with prediction. The arguments above do not prove that nothing interesting can be said about possible futures of science. In fact, given the main objectives of futures research, we have reasons to think that the focus on predicting of particular occurrences puts the cart before the horse.
First, notice that the occurrence of a particular event usually depends on the surrounding context. This is the very feature that makes them difficult to predict. As Staley points out, “events are so dependent on individual actions, accident, contingency, context, and any one of countless other variables, [that] venturing a prediction about future events is doomed from the start” (2002, 75). Secondly, decisions affect the future. In order to make meaningful decisions, we have to understand the consequences of those decisions. This is possible only if we understand the possible contexts where the consequences of the decisions unfold. It follows that knowledge about the possible context of the future is epistemically prior to knowledge of particular events. Given these two observations, it seems that we should study possible contexts (or “structures” as I call them) where events might take place in the future.
If the reader is interested in seeing how scenarios about the future of science can be built, I discuss the issue in this post: