Chris Haufe’s Fruitfulness tackles an undoubtedly important topic: how to gauge an idea’s scientific promise or potential for further fruitful exploration. Notwithstanding its practical relevance, especially for working scientists (as well as funding bodies), philosophers of science have treated it somewhat negligently.

The publication of this book is timely. Various commentators have, for instance, diagnosed a crisis in fundamental physics, calling for studying bold new ideas to overcome what they perceive as a period of relative stagnancy. But, as Peirce eloquently put it, ‘proposals for hypotheses inundate us in an overwhelming flood’ (Weiss et al. [1958], p. 5.602). Which are the auspicious proposals that, in light of scarce (mental or material) resources, merit closer scrutiny?

Haufe’s engaging monograph is therefore a welcome addition to the philosophy of science literature. It’s highly readable with a consistent thread running throughout the book. Haufe intersperses a largely academic style of writing with passages that are highly casual, humorous, and sometimes even self-deprecating. Some readers will find this refreshing, others unnecessarily distracting. The book must be praised for its methodological diversity and broadness in approach: it weaves together threads from Kuhn and philosophy of language; ranges across topics concerning problem-solving, analogy, natural kinds, inductive inference, and historiography; and breathes life into abstract discussions with case studies from physics, mathematics, biology, and palaeontology.

We first summarize Haufe’s main thoughts, as they are successively expounded in the chapters of the book, before closing with some critical comments.

Chapter 1 introduces the book’s main themes and ideas. Chapter 2 lays out the problem Haufe is concerned with throughout the book: the puzzle of promise. The puzzle arises from the notion of paradigm change in Kuhn’s philosophy: how to epistemically justify the ‘future promise’ of a new paradigm (and adherence to it) when the old paradigm has already proven its puzzle-solving capacity whereas the new one has yet to do so. In The Structure of Scientific Revolutions, Kuhn ([1996]) had left the puzzle open, appealing to bare ‘faith’. In that book’s postscript, and in his ‘Objectivity, Value Judgment, and Theory Choice’ (Kuhn [1977]), he appeared to make progress on this unpalatable answer. There, he suggested that paradigm choice proceeds on the basis of the standard theory choice criteria (accuracy, consistency, scope, simplicity, and fruitfulness). Haufe complains that the only rationale Kuhn gives for why the satisfaction of these criteria should increase confidence in a paradigm’s future promise is that scientists are rewarded by their community for maximising the satisfaction of these criteria. On this rationale, Haufe argues, anything that happens to result in reward for scientists may be plugged into the place of the standard theoretical virtues, for example, hilariousness or complexity. He hence dismisses what at first blush looked like an improvement: according to Haufe, Kuhn’s attempt to salvage the rationality of theory choice amounts to no more than faith dressed in new clothes (p. 24). Still, Haufe sees the beginning of an answer to the puzzle in the set-up of problems by a new paradigm.

In chapter 3, Haufe elaborates on the idea that fertility isn’t driven by solved problems (as Kuhn suggested) but rather by the imposition of a novel set-up or structure of problems, which promises solvability. A new paradigm, for Haufe, defines a ‘family of solvable problems’ that are then to be explored in the life of a paradigm (p. 45). He takes issue with Kuhn’s suggestion that scientists learn to appreciate the future promise of a new paradigm by acquiring ‘similarity relations’ that hold between the problems defined by a new paradigm. For Haufe, the relation between the problems set out by a paradigm isn’t learned—more specifically, it isn’t learned by ‘seeing’ things differently—but imposed by conscious decision (p. 52). Problems are determined as belonging to a class of problems via argument patterns (in the sense of Kitcher [1989]), and solvability of class members then becomes solvability of the whole class. The applicability of Newtonian celestial mechanics to not just elliptic orbits but to orbits of the form of any conic section is a case in point (p. 57). The imposition of structure may of course fail. Even then, failure may teach researchers important lessons about a domain, or about the exemplar’s conceptual toolkit and how it works (pp. 61f). Haufe goes as far as suggesting that even success need not be grounded by real world relations (p. 59).

Chapter 4 unpacks the ‘emergence of exemplars’: how certain problem-solving attempts gain the status of ‘samples’ of problem-solving that embody promising strategies (and hence deserve further scrutiny and imitation). Haufe’s motivating examples are taken from the history of seventeenth-century mathematics, especially early, auspicious—but theoretically and/or mathematically still unsatisfactory or otherwise limited—results that would have to await the fully fledged calculus to be acceptable. Yet, these results spurred mathematicians’ creative imagination and the ablest of them further pursued those (half-baked) ideas and techniques. This pursuit once again poses the puzzle of promise: why did leading scholars adopt those novel and as yet unproven ideas and techniques? Haufe’s answer lies in the notion of exemplification (inspired by Goodman [1983]): a scientific result, no matter how tentative and limited, may possess or display some features that seem salient for a wider range of problems. Thanks to such exemplification, the potential problem-solving power—or, in Haufe’s parlance, problem-structuring idea—invites its transfer, the application of its ‘spirit’, to a new domain. Practitioners thus impose this (often implicit) ‘structure’ or ‘schema’ (p. 105) on new problems within that other domain—an act of discretion, rather than one owed to any necessity. Those structures or schemas (not necessarily conceived of in formal terms, as Haufe’s example of Darwinian evolutionary reasoning illustrates; p. 101) are supposed to guide a subsequent research agenda. They serve—and, as Haufe stresses, ought to serve—as tools for investigation, by ordering phenomena, raising core questions, and proffering strategies and techniques for tackling them.

In chapter 5, Haufe turns to the notion of a frame, which he borrows from Elisabeth Camp: a frame is a collection of ‘open-ended tools for assimilating new information and for generating hypotheses about undiscovered features and causal structures’ (p. 126). It comprises ‘some set of ordering principles through which practitioners can express problems that they can work on’ (p. 108). Thanks to frames, a strand of research can flourish in a wider community; frames furnish ‘a generalized means of structuring investigations so as to produce a result upon which other members of the field can build’ (p. 111). Their ordering principles can be abstract (for example, the structure of mathematical equations, as in the case of electrostatics; p. 113), more qualitative frameworks (such as the corpuscular theory of light; p. 115), or even informal analogies (as in Maxwell’s attempts to model electrodynamics on fluids; p. 116). As a repository of ‘some method of investigation’ (p. 117)—useful questions and sketched strategies for finding answers—frames are supposed to indicate a tentative way forward. They thus encapsulate the previously mentioned capacity of some ideas for thrilling scientists and for stimulating them to explore how an idea might carry over to other domains. An exemplar that seems apt to shed light on a novel problem, according to Haufe, bestows ‘legitimacy’ on the problem: it ‘can be set up in a way that makes it solvable’ (p. 110). An example from palaeobiology, dealing with the role and impact of mass extinctions, further illustrates the notion (p. 126). For Haufe, the significance of frames can’t be overestimated, both descriptively and normatively. The guidance and inspiration that emanate from them ‘are the beating heart of science’ (p. 140). Since frames play such a central role for decision-making in research (that is, for determining which ideas to pursue) and concomitantly for scientific rationality tout court, Haufe concludes, ‘we need a different epistemological toolkit’ (p. 140)—one that extricates itself from the traditional focus on truth and austere epistemic justification.

Chapter 6 zooms in on the titular topic of fruitfulness. Haufe ties it to ‘unexpected benefits’ (p. 142). Building on remarks by Poincaré, Frege, and Hilbert on fruitful ideas in mathematics, Haufe proposes that ‘Fruitfulness in the context of research […] is about the unexpected production of multiple families of solvable problems’ (p. 143). ‘In place of the normativity of truth’ (p. 134) or correctness, which ‘per se offers almost nothing to our efforts to pursue other research questions’ (p. 138), scientists first and foremost prize ‘whatever they believe will allow them to structure research problems so as to make them solvable’ (p. 134). Haufe explains the persistence or entrenchment of frames in the scientific community in terms of demonstrated fruitfulness (p. 153). But how exactly does fruitfulness work? To flesh this out, he draws on metaphors and analogies, following Kuhn (to whom, however, Haufe imputes—to our minds, unfairly—a strong psychologism; p.147). Haufe rightly reminds readers of Poincaré’s astute observation that even ‘the act of classifying two experimental trials as two runs of the same experiment is an act of analogy’ (p. 47). Such deliberative judgements, based on comparisons, similes, and analogies are indeed ubiquitous in science; they form an integral part of scientific rationality that (as Kuhn also underscored) doesn’t reduce to rules in a mechanical calculus. Haufe here convincingly points to Darwin’s argument from domestication in the Origin for illustration.

In chapter 7, Haufe turns his attention to epistemic warrant for judging the future promise of research frames. The type of epistemic warrant he is after does not concern belief but rather use (pp. 180f.). Before presenting this alternative in more detail, Haufe attacks what he considers to be traditional forms of epistemic warrant. In particular, he argues that realist explanations of novel success are inadequate because scientists don’t seem to care much about novel success nor, by extension, about truth (pp. 189–91). Haufe’s own proposal for an epistemic warrant concerning future promise is inspired by Poincare’s writings and explores the notion of warranted generalization in terms of warranted analogy or metaphor (p. 191). Essentially, analogies or metaphors allow scientists to expand their early problem-solving achievements to further problems. Controversially, Haufe maintains that the ‘validity of analogy’ is ‘largely a matter of agreement within the community of practitioners’, because it is they who have to decide which similarities between problems are salient and which are useful (p. 196). He also resists the idea that generalizations must truthfully reflect the facts of the world and instead views generalizations as classification attempts that involve value judgements about what kinds of similarities matter (pp. 201–4). Inductive projection is thus not about the actual properties of unexamined objects but rather about the community’s decision to highlight analogies between class members and new objects (p. 205). Whether analogies are apt—that is, whether they are suited to guide inquiry—can be judged by practitioners ‘more or less instantaneously’ (p. 213). Indeed, Haufe seems to attribute a quasi-Duhemian ‘sense’ for what frames and analogies facilitate inquiry (p. 218).

In chapter 8, Haufe argues that theoretical virtues such as simplicity and symmetry, which he refers to as ‘aesthetic’, are epistemic because they promote a frame’s fruitfulness ‘by increasing the solvability of problems’ (p. 222). Because they do so, they are immediately recognizable signs of the ‘aptness’ of a frame and don’t require previous experience with that frame (p. 224). To support this view, Haufe identifies (following Quine) ‘familiarity’ as an important dimension of understanding; it reduces cognitive effort in problem-solving (pp. 224–28). Aesthetic virtues likewise increase solvability, according to Haufe, because they work just like familiarity (p. 242). What really distinguishes aesthetic virtues like simplicity from familiarity is that they ‘achieve in an instant that what familiarity requires past experience to accomplish’ (p. 243). He goes on to argue that this view has an advantage over realist views, which seek to connect aesthetic virtue to truth, because only his view easily accommodates the diversity of simplicity judgements (p. 249). In essence—albeit not in letter—Haufe defends a pragmatist account of theoretical virtues: an aesthetically appealing theory’s success ‘has more to do with what we are good at using than it does with what nature is like’ (p. 249); virtues need not correlate with truth but only must make a theory ‘easier to use’ (p. 255).

The book closes with a critical reflection on externalistic historiography (chapter 9), according to which discoveries are the outcome of contingent external factors, such as the political climate at the time. Haufe takes this view seriously and argues that ‘close shaves’—that is, discoveries that may not have come to pass had things been only slightly different—are no threat to his view. This, according to Haufe, is what fruitfulness furnishes, namely, decision-making based on fruitfulness safeguards a sense of rationality for research that isn’t affected by worries about close shaves: ‘The carefully reasoned pursuit of fruitfulness per se can promote progress independently of what variety of fruit pops up’ (p. 268). What matters, to Haufe’s mind, are less the particular results and discoveries science produces, and more that science tends to produce scientifically valuable results and discoveries. Haufe’s key, and once more squarely Kuhnian, thought is to regard scientific communities ‘as highly effective systems for optimizing and promulgating problem-solving practices’ (p. 275). He concludes that if we find compelling his case for the rationality of pursuing fruitful ideas, as understood in the foregoing chapters, then the rationality of science has been vindicated as sufficiently robust and (to a satisfactory extent) freed from the contingencies of happenstance often witnessed in actual history.

Readers will surely benefit from Haufe’s book: it’s an entertaining and fruitful read, bound to stimulate further reflection on this crucial topic. As reviewers working in relevant areas within philosophy of science, however, we’d be remiss not to draw attention to some of the book’s shortcomings. Three in particular stand out.

First, even though the puzzle of fruitfulness may be especially severe for Kuhn’s account of science, the problem is in fact a general one, and one that has already been picked up in the existing literature on pursuit-worthiness (for a comprehensive literature review, see Duerr and Fischer [2025]). Even some more ‘classical’ work—Lakatos on heuristics, Laudan on problem-solving, McMullin on fertility—would have been directly relevant to exploring solutions to the puzzle. In particular, Laudan’s ([1977]) distinction between the context of acceptance and the context of pursuit very much foreshadows Haufe’s turn away from classical theory acceptance toward his concern with the puzzle of promise.

Second, Haufe also commits some exegetical blunders in his reading of Kuhn. For example, contrary to claims throughout the book, Kuhn repeatedly disavowed the view that theory change is irrational (for example, in his exchanges with Feyerabend and Lakatos; see Hoyningen-Huene [1995]). Instead, Kuhn explicitly intended to depict science as the best example of a rational enterprise (see, for example, Schindler [2024]). The view of theory choice he articulated in his ‘Objectivity’ chapter is arguably best described as admitting of multiple, rational ways of selecting a theory (see Okasha [2011]). There are many other examples of contentious readings of Kuhn here: Kuhn didn’t reduce theoretical virtues to the social reward structure of science (chapter 2); he didn’t think that perceptual change causes paradigm change (chapter 6); and he didn’t think that new paradigms could not boast of any problem-solving successes (chapter 2).

In general, we note that Haufe pays insufficient attention to existing literature relevant to his project, for example, the extant literature on problem solving (again, Laudan!), theory choice, novel success, analogy and metaphor, and natural kinds. An especially unfortunate omission is Mary Hesse’s ground-breaking and influential work on analogies and metaphors in science (and scientific modelling in particular; for details and further references, see Hesse [1970], [2000]). Haufe’s neglect of the literature is often undermines his own claims. For instance, his discussion of realist accounts of theory choice and novel success (chapter 7) leans heavily on studies by the historian Stephen Brush. With Brush, Haufe singles out Mendeleev’s predictions of new chemical elements as the only case where novel success really mattered to scientists. Unfortunately for Haufe, however, there has been a large swath of literature both reconstruing novelty in non-temporal terms (making Brush’s examples consistent with realist epistemology) and disputing the role of temporal predictive success in the Mendeleev case (see, for example, Scerri and Worrall [2001]).

Haufe’s own proposal for solving the puzzle of promise suffers from significant lacunae, too. Despite the centrality of problem solving in this account, Haufe says little about what he takes to be a scientific problem and, worse, what makes a problem solvable. Assuming a wide Kuhnian notion of a problem—which comprises the problem of matching theory and evidence—we might say that a problem of this kind is solved when it leads to empirical success. But Haufe eschews any talk about empirical fit or even truth. He is much concerned with scientists wanting ‘a theory by which to work’ (p. 104). Unfortunately, he has almost nothing to say about how to get a theory that actually works.

Relatedly, Haufe declares knowledge an aim of science, but it’s unclear how he wants us to think of knowledge if not with reference to truth or at least empirical adequacy. Here, he could easily have helped himself to the burgeoning literature on understanding (for example, Elgin [2017]) and progress in understanding (Dellsén [2016]; De Regt [2017]). Similar remarks apply to Haufe’s discussion of theoretical virtues. He describes them in thoroughly pragmatic terms while still referring to them as ‘epistemic’ (chapter 8). Haufe seems to think that the virtues are epistemic because they indicate problem-solving promise; this is underdeveloped and would have profited from an engagement with the pragmatic accounts of knowledge by Peirce, Dewey, and others.

Throughout the book, Haufe insists that solved problems don’t help us with the puzzle of promise (contra Kuhn). But he equivocates between two claims: solved problems cannot fuel future promise whatsoever, or solved problems cannot provide the complete answer to the puzzle. The latter claim seems trivial, since there is more to a frame or paradigm than solved puzzles. The former claim, by contrast, seems obviously wrong. On Kuhn’s ([1996], p. 172) view, paradigms as ‘exemplary past achievements’ come with impressive successes (historically epitomized by, for example, Newton’s Principia and Darwin’s Origin). Plausibly, early exemplars give practitioners inductive reasons to hope that the paradigm will be successful in the future as well (see Schindler [2024]). Although Haufe talks about inductive inference in his book, he reconstructs it in sociological and relativist terms (chapter 7).

It bears some irony that Haufe’s overall account ends up more sociological and relativistic than Kuhn’s, the principal target of the book. But whereas Kuhn suggested that scientists acquire (real world) similarity relations, for Haufe set-ups are ‘imposed’ on problems—a sheer decree on the scientist’s part—and the aptness of analogies between problems come down to community decisions (chapter 7).

Despite our critical remarks, we think Haufe deserves credit for highlighting the puzzle of promise, and for trying to develop new ways of addressing it. Haufe’s discussion is engaging and the chapters of the book unfurl a coherent narrative. Whatever the ultimate verdict on the solution the book offers, it’s systematic and consistent in its unabashed pragmatism. It deserves to be read by anybody willing to think more deeply about the puzzle of promise and the wider issue of pursuit-worthiness.

Samuel Schindler
Aarhus University
samuel.schindler@css.au.dk

Patrick M. Duerr
University of Tübingen
patrick.duerr@uni-tuebingen.de

References

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