Introduction
Science requires resources. This limits the number of research programs[1] that can be initiated and kept alive. Due to this, we have to make decisions concerning which research programs to pursue. This generates the problem of pursuitworthiness. We have to identify those research programs that are worthy of pursuit. On what criteria can the identification be based?
The problem is difficult because we (most likely) do not want to define pursuitworthiness in terms of the actual success of a research program. A novel research program cannot have much actual success before it is actually developed. Still, we most likely wish to develop novel lines of research. This means that traditional accounts of theory-choice and scientific rationality are not straightforwardly applicable to pursuitworthiness, as they focus on the actual features of research programs (Whitt 1990, 467). To see the depth of the problem, we may notice that even if we focus solely on the actual and mature research programs, the problem of pursuitworthiness is not automatically solved. The actual success of a program thus far does not guarantee that it will be successful in solving new problems in the future or that it is better than some other candidate research program that we could reasonably develop using the available resources. As Nickles puts it, “What justifies a scientist’s decision about what to work on now, or next, is not its past—its confirmation track record—so much as what it promises for future innovation” (2006, 161). Moreover, the mere continuation of existing research programs decreases the robustness of scientific knowledge, as robustness requires that we have alternative approaches available if our best theories face crises in the future (Šešelja and Straßer 2014). This means that the criterion that the actual success (thus far) defines pursuitworthiness is just one among many possible criteria whose merits need to be discussed in detail.
There have been many suggestions concerning what criteria can be used to identify pursuitworthiness. Shaw (2022, 104) summarizes some of the central suggestions:
“(1) An idea is pursuitworthy if it is relatively likely is it to give rise to interesting extensions, shows promise of being able to handle the outstanding problems (inconsistencies, anomalies, etc.) in the field, unify hitherto diverse areas, or open up entirely new territory (McMullin, 1976, pp. 423–424).
(2) An idea is pursuitworthy if it is empirically fertile and conceptually viable (Whitt, 1992, 620).
(3) An idea is pursuitworthy iff it is most likely to be true at the least expenditure of time, vitality, etc. (see McKaughan, 2008, 452).
(4) An idea is (initially) pursuitworthy iff it possesses potential explanatory power, potential inferential density, potential consistency, and a programmatic character (Šešelja & Straßer, 2014, 3123).
(5) An idea is pursuitworthy iff there is a set of questions that it seeks to answer, a set of instructions that it seeks to impose with respect to these answers, is justified in raising these questions and imposing these instructions, and in believing that the idea provides answers to these questions in a way that satisfies these instructions (Achinstein, 1993, p. 111).
(6) An idea is pursuitworthy iff is more likely to provide some exemplary practices which are repeatable, provide a reliable framework for further investigation to solve the unsolved problems, and generate more testable research problems across more different areas (or disciplines) (Shan, 2020, p. 181).
(7) An idea is pursuitworthy iff its pursuit is conducive to a set of goals (Šešelja et al., 2012).”
As we see, the analysis of pursuitworthiness is usually conducted in terms of search for features of research programs that indicate that they are promising or potential. In this post, I argue that the merits of the criteria need to be discussed within a wider scheme. I will not criticize any suggested criterion as such, but I will discuss how the discourse concerning pursuitworthiness lacks a systematic perspective on the future. I suggest that the merits of the criteria need to be analyzed in terms of futures research and possible futures in general. Futures research is a field that concerns possible and desirable futures and our cognitions about those futures. There are specific needs and motivations that shape futures research, and the discussion on pursuitworthiness, which is a discussion about estimations of the future, would greatly benefit from closer contact with these goals and motivations. I argue that how we should think about pursuitworthiness depends on how we should conceive and reason about the future in general.
Pursuitworthiness and Possible Futures of Science
In futures research, possible, probable, and desirable futures are studied (Amara 1974; Bell 2009). An essential component in the mapping of futures is the critical study of our own conceptions that ground different scenarios of the future (Bell 2009; Inayatullah 1998; Inayatullah & Milojevic 2015). As Bell points out, “[t]he exploration of possible futures includes trying to look at the present in new and different ways, often deliberately breaking out of the straitjacket of conventional, orthodox, or traditional thinking and taking unusual, even unpopular perspectives” (2009, p. 76-77). The study of the future is grounded on the assumptions that
(i) the future is difficult to estimate (uncertainty),
(ii) decisions affect the future (accountability),
(iii) the most desirable futures may not be causally accessible (realism).
Futures research, therefore, requires that
(a) many possible futures are mapped (to account for i and ii),
(b) the desirability of the possible futures is evaluated (to account for ii), and
(c) our preferences have a reality-check (to account for iii).
The basic assumptions of the study of the future are rather trivial. However, their consequences are far from trivial and their value stems from their ability to guide systematic analysis of possible futures, as we will see. Many future-oriented discourses, such as the one on pursuitworthiness, can be framed and developed in terms of these assumptions.
In addition to basic assumptions, the two main objectives of futures research are the following:
(A) “enhancing understanding: of the causal processes, connections and logical sequences underlying events — thus uncovering how a future state of the world may unfold”.
(B) “challenging conventional thinking in order to reframe perceptions and change the mindsets of those within organizations”.
Given A and B, we “can provide information, ideas and stimuli to support a third objective; better decision making and strategic planning”. (Wright et al. 2013, 631.)
Discussions on pursuitworthiness concern possible futures on two levels. The first-order level concerns which research programs are worthy of pursuit, given our current scientific knowledge. On this level, we wish to assess the possible futures of research programs in terms of what we already know, what our levels of confidence are, and what gaps in knowledge we explicitly recognize. First-order assessments of pursuitworthiness are made by funding agencies, other decision-makers, and even individual scientists.[2] The second-order level concerns the dynamics of scientific development and the pursuitworthiness of programs in the scheme of these dynamics. On this level, we wish to assess the criteria of pursuitworthiness against the background of science as an epistemic institution with historical dynamics, goals, values, and accountability for wider society. We wish to understand why pursuitworthiness needs to be assessed and how it can be assessed, given the dynamics of the development of science.
In the philosophical literature, the second-order level is often discussed only implicitly and merely to frame the analysis of the first-order level criteria. This is a shortcoming due to the lack of systematicity and due to the fact that the explicit considerations of second-order level dynamics are essential to solve a puzzle concerning the fundamental unpredictability of science, formulated recently in terms of pursuitworthiness by Shaw (2022). However, the literature on pursuitworthiness is rich in its suggestions concerning the second-order level and incorporates insights similar to those that futures research seek.
An overreaching theme in the literature on pursuitworthiness is the view that, in science, new lines of research and the prospects of existing lines need to be constantly assessed. As Shaw notes, “most (if not all) proponents of a logic of pursuit want to allow space for some pluralism” (2022, 104). In the relatively early discussions on pursuitworthiness, the value and need for pluralism were framed as facts of history of science that needs to be appreciated in the spirit of historically oriented science. For example, Laudan, following Feyerabend[3], notes that pursuitworthiness is a worthy issue because every new research tradition occurs in circumstances where they are less acceptable than their rivals. Another side of the coin, according to Laudan, is the historical fact that a scientist can work in two different traditions. (Laudan 1977, 110). Also, Achinstein simply notes that “Sometimes a scientist presents a new theory without attempting to argue that it is true or even probable [–]” and associates this phenomenon with the need to allocate resources (1993, 90).
More recently, the discussion on pursuitworthiness has focused on more nuanced motivations and reasons behind the pluralistic aspirations that frame the analyses on pursuitworthiness.
Šešelja and Straßer rely on their approach to pursuitworthiness on the notion of scientific crisis. “[T]he history of science reveals that scientific knowledge is highly dynamic and we shouldn’t be all too assured with the theories we have accepted. Not just is it the case that theories often have to be altered and adjusted, but sometimes they have to be entirely replaced.” (Šešelja & Straßer 2014, 3112). The need for plurality in pursuits stems from the fact that “these times of crisis we do not want to face empty-handed” (Šešelja & Straßer 2014, 3112). Šešelja and Straßer argue that we need to have robust scientific knowledge that is able to maintain performance in the face of perturbations and uncertainty. Because any theory may face crises, we need more than robust theories. We need robust scientific knowledge as a whole. From this perspective, “scientific knowledge is composed and structured by layers of more and more entrenched theories” (Šešelja & Straßer 2014, 3113). In addition to accepted theories, we need a layer of “alternative theories that may in times of crisis offer good backups for the accepted theories, or that may under further development eventually surpass the currently accepted theories” (Šešelja & Straßer 2014, 3113). Pursuitworthy theories do not have to be justified, but they have to be potentially epistemically justified and contribute to the robustness of scientific knowledge.
It is interesting to note that Šešelja and Straßer rely on three (implicit) assumptions about the future that are also at the core of futures research. First, there are uncertainties about the future. History indicates that even our best theories may face serious crises (uncertainty). Secondly, our actions should enable us to prepare for and react to future changes. Pluralism in pursuits is a condition that enables us to respond to multiple possible futures, even the ones that generate scientific crises (accountability). Thirdly, we need to prepare for futures that would show that our best efforts today are fruitless (realism).
The analysis of Šešelja and Straßer also matches the goals of futures research. It relies on (presumed) patterns in scientific development. There have been crises and there might be crises in the future. The analysis also challenges a conventional view of scientific knowledge as consisting of accepted theories. What also matters for our future aspirations are alternative backup theories.
The themes that arise in Šešelja and Straßer (2014) repeatably occur in the second-order level framing of analyses of pursuitworthiness. For example, Nickles argues that “[g]ood research is highly adaptive to changing situations, including local contingencies” and that epistemic appraisal (EA) is not highly adaptive in this way (2006, 161—162). Therefore, we need heuristic appraisal that evaluates the future potential of a claim, technique, proposal, etc. Again, we see the assumptions of uncertainty, accountability, and realism. Moreover, Nickles relies on historical considerations in his argument for the need for heuristic appraisal. He points out that “[s]ome of our most fertile theories, models, and programs have been known in advance to be false and even inconsistent (or otherwise incoherent) at some point” and “there are also plenty of examples in which a presumably true theory or correct result is unfruitful as a future research site” (Nickles 2006, 162). Here, patterns of historical development inform the construction of tools for heuristic appraisal that enable us to react to future changes and contingencies. Nickels also challenges conventional thinking by arguing that “standard EA leaves us with a severely limited account of scientific decision-making, even when the key materials are already assembled and on the table for appraisal” (2006, 159).
Accountability is a topic that has been emphasized in analyses of pursuitworthiness, especially when the discussions widen the scope from epistemic promise to the wider set of values in a society. For example, Kitcher’s well-ordered science, scientific projects are analyzed through moral constraints and preferences of citizens (Kitcher 2001). Kitcher argues that “Even when informed scientists and policymakers try to think broadly about research options and how they might promote the collective good [–], the visions are still partial and limited” (2004, 221). Kitchers suggests that “we need a place for a more synthetic view of the possible developments of our current sciences. Instead of jumping from one partial perspective to the next, we should create a space in which the entire range of our inquiries can be soberly appraised.” (2004, 221.) Again, the possible futures of science need to be constructed in terms of scenarios that take into account more than the epistemic promise of the research program pursued. Scientific actions affect the future beyond the epistemic qualities of science and the actions should be evaluated accordingly.
This relationship between pursuitworthiness and the required richness of scenarios of the future can be clarified and systematized by relying on the definition of pursuitworthiness by Šešelja et al. (2012). They argue that
“It is rational for Y to pursue X if and only if pursuing X is (sufficiently/most/etc.) conducive of the set of goals Z” (Šešelja et al. 2012, 53).
Different future scenarios are relevant for the pursuitworthiness depending on the nature of Y, X, and Z. Šešelja et al. argue that “[b]y interpreting each of the variables X,Y,Z in a different way, we can obtain different notions of pursuit worthiness” (2022, 53). Of course, not all interpretations are equally interesting.[4] However, we should not limit Z to epistemic goals. Šešelja et al. argue that “scientific inquiry as a part of the scientific practice may concern a broader spectrum of non-epistemic (or non-cognitive) goals as well, such as ethical, social or political goals” (2012, 64). Assessments of pursuitworthiness require that we take into account many aspects of possible futures on which the pursuit of a scientific research program may have an impact.
Thus far, we have seen how analyses of pursuitworthiness require a rich mapping of possible futures of science, relevant considerations ranging from epistemic to social values to moral constraints. We have noted that the richness of future scenarios would benefit our assessments of pursuitworthiness. However, there is a problem. It appears that there are fundamental obstacles in the estimating of possible futures of science when it comes to epistemic aspects of science. It seems that the difficult question is not how to get beyond the epistemic assessment of pursuitworthiness but how to get the epistemic assessment off the ground in the first place. In the next section, I introduce the problem following Shaw (2022). The problem is that it seems that we should be able to predict the future of science in order to assess pursuitworthiness, but there are fundamental obstacles to predicting the future of science. This threatens the whole notion of pursuitworthiness. In what follows, I sketch a solution to the problem by noting that (a) analyses of pursuitworthiness make assumptions about the dynamics of development of science, and (b) scenarios of the future can be constructed by systematizing these assumptions.
Unpredictability of Science
We have seen that analyses of pursuitworthiness are often 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. However, Shaw (2022, 104) points out that the contents of the analyses 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 and 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. 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 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 some general solution to the estimating the future of science in many different contexts.
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.)
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. 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 other questions are futile. 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 an answer to our question (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, there still remain many interesting questions we can ask with respect to the future of science. The arguments against the possibility of estimating the future of science are therefore seriously limited in their scope.
Thirdly, one crucial element in the arguments is the assumption that the goal of the study of the future is to predict particular events, 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 golden 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. 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 the 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, and this means that knowledge about the general 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 will call them below) where events might take place in the future.
Possible Futures and Pursuitworthiness
In a previous post (HERE), I have argued that we can study the possible future contexts of science and we can do this by systematizing our views and theories of science. Philosophy of science is a rich source of different views and theories of science and therefore enables us to build rich taxonomies of possible future contexts of science. Understanding different possible futures of science will enable us to critically assess criteria for pursuitworthiness in the wider scheme of possible futures. Once we have a rich set of scenarios of the future, we can better assess the merits of criteria of pursuitworthiness.
First, we can assess the scope of a criterion by explicating its assumptions concerning the dynamics of science and analyzing how many scenarios are compatible with these assumptions. For example, a criterion that relies heavily on the continuity of a current research program would be limited in its scope, as the criterion would not allow us to understand pursuitworthiness in the context of a scientific crisis. Limited scope is not necessarily a bad thing. For example, some scenarios might be such that, no matter what we do, we cannot prepare for them (for example, a scenario of a sudden and fundamental crisis), not to mention scenarios that are far-fetched or incredible. However, wide scope is, in principle, a valuable feature, as it enables us to act and react towards many possible outcomes. This matches the assumptions of uncertainty, accountability, and realism, and enables us to see multiple possible causal patterns and thus challenge conventional thinking. This brings us to the next point.
Secondly, we may ask how well a criterion enables us to act towards desirable futures. By a desirable future, we do not mean here a future that contains a scientific result we wish to achieve. Rather, we mean a future where science works, whatever this means. For example, Šešelja and Straßer’s idea of robust science suggests that a desirable science is one where a possible crisis can be faced in a resourceful way. Taxonomies of scenarios are maps that enable us to see possible future conditions and see how those conditions might be achieved. An overview of possible futures improves our ability to compare the desirability of different future outcomes and to see how different assumptions about science shape how we understand the notion of well-working science. Once we have identified desirable futures by constructing scenarios, we can assess to what extent a criterion of pursuitworthiness enables us to act towards these futures. For example, a criterion that relies heavily on the continuity of a current research program would not enable us to generate a crisis in an orderly manner as it would deny or remain silent about the possible future crises.
Thirdly, the construction of scenarios of the future does not merely use philosophical accounts (or mere assumption) as theoretical bases but also enables us to critically evaluate the philosophical accounts. There are ambiguities and blind spots which become visible when we construct scenarios of the future. In this way, future-oriented thinking can open new perspectives and lines of research concerning the development of science. The difficulties in the estimating of the future of science reveal difficulties in our understanding of the development and workings of science.
To sum up, assessing the criteria of pursuitworthiness against the wider scheme of futures has many advantages. First, it enables us to manage and work with uncertainty by comparing the scope of a criterion to the scope of possible futures. Secondly, it enables accountability by revealing the scope a chosen criterion. Whether we like it or not, by choosing a criterion, we steer towards particular futures. Thirdly, it enables us to maintain realism by (i) mapping scenarios where our choices of what to pursuit, no matter how they are made, do not achieve what we wish for, and (ii) by revealing the intertwined nature of a desirable science and its possible futures. Finally, the wider scheme of futures enables us to identify multiple possible causal patterns and to challenge and critically assess different accounts and assumptions concerning science.
Finally, we see that the merits of criteria of pursuitworthiness are not essentially dependent on our ability to predict the future of science. Even though science does change and the existing cognitive horizon may be abandoned, we can still say many interesting things about the possible future structures of science. In fact, change and its possibly radical nature do not forbid futures research but motivate it and make it possible. How science changes and how radical these possible changes are are the kinds of questions that futures research assess when it constructs many scenarios of the future. However, as Shaw (2022) has pointed out, the current criteria of pursuitworthiness in the literature quite likely depend too heavily on the existing cognitive horizon. Given the wider scheme of futures, we would wish to have more plurality in the suggestions.
References
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Feyerabend, P. (1993 [1975]). Against method. London: Verso Books.
Finocchiaro, Maurice A. (1973). History of Science as Explanation. Wayne State University Press.
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Šešelja, D., Kosolosky, L., & Straßer, C. (2012). ”The rationality of scientific reasoning in the context of pursuit: Drawing appropriate distinctions”. Philosophica 86. 51–82.
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[1] In this post, I use the term “research program” in a non-technical sense to refer to any systematic research that attempts to achieve something: a new theory, model, experimental result, paradigm, technology, and so on. I make more detailed distinctions when it matters to our views on the future.
[2] See Šešelja et al. (2012).
[3] As we will see, Feyerabend can be viewed as a limiting case of motivating first-order level discussion on pursuitworthiness because he thought that no substantial criteria for pursuitworthiness can be found (see Shaw 2022).
[4] For example, it might be that a person (Y) would fabricate data (X) to become famous (Z) but this is hardly an interesting analysis of pursuitworthiness.