Shapin draws attention to professional vested interests that are internal to science and research, but not strictly cognitive. Active scientists know these very well as they determine the ongoing discussions, at the moving front of research, with reviewers 'from other schools' at journals, grant review committees, scientifc committees selecting conference contributions (selection of main speakers and of oral abstract presentations), academic promotions committees and decisions who writes or contributes to textbooks. All of these judgements determine what 'we' hold to be 'good' research or 'the best' research at some point in time, which over my 40-year career developed and changed rather quickly (Miedema, 2012). An outstanding analysis of the diversity of private, professional, cultural, social and economic factors that infuence the practice of inquiry and knowledge making is Gerald Geison's study '*The Private Science of Louis Pasteur'.* (Geison, 1995) This book was by many especially French scientist considered to be debunking Pasteur. It was published, at the same time as more hagiographic biographies at the centenary of his death in 1995, but by experts highly praised because it provides deep and detailed insights how knowledge, in basic but also in applied biomedical research with enormous societal and economic impact, was and is produced. In a critical, humiliating review of Geison's book, Max Perutz (1914–2002), who was a famous biophysicist, defended Pasteur, against Geison's demonstrations and judgements of Pasteur's obvious foul play (Perutz, 1995). The bottom-line of the defence was that in the end Pasteur had been proven right, only the facts count in Perutz' opinion. The real issue at stake, that clearly surfaced in the exchange that followed in the NYRB, was that an outsider, not a man or woman from the lab, apparently not with 'pious reverence' and excessive respect, was messing with men of science and its methods (Miedema, 2012). Other writers of recent history of science, such as Crewdson have been overly critical, for instance regarding the role of Robert Gallo, in a study of the discovery of HIV, the aids virus in 1983 (Crewdson, 2002). Crewdson on the other hand has undue sympathy for the 'underdog' in this dispute that involved massive professional reputation including a 2008 Nobel prize, national politics and economic interests (Miedema, 2002).

Shapin has since 1982, written a number of classical highly infuential journal articles and books about the practice of science and the production of knowledge in the seventeenth century and in our times by doing in depth research using historical and sociological methods in which all of the above topics, theories and problems are addressed (Shapin, 1994, 1996, 2008; Shapin et al., 1985) In the last pages Shapin provides a balanced discussion of how to view the infuence of external and noncognitive factors on knowledge production. Some researchers simply regard it as wrong based on the ideal of objectivity and value free science and studies in sociology or history that reveal these infuences are considered damaging and 'aspersions'. Some regard these infuences as realistic, it happens and is diffcult to avoid, but they are per defnition corrupt because science is, and its institutions are in that way being hijacked by all kinds of powerful politically and socially organized groups and their interests. Shapin regards these views as 'a misunderstanding' as external values and concepts have had and may have benefcial effects on the growth of knowledge. Opening up science to less powerful publics has these risks and as discussed in depth in Chap. 5, it will require continuous debate to resist the capture of science by the economic powers in society.

# *The Myths of Science: Frontstage and Backstage*

Humans and scientist alike need certainty, a logical method, an algorithm, with timeless and thus objective foundations. But the Quest for Certainty has failed. We have in reaction to this in the 1990s seen academic debates and worries about loss of certainty and foundation of scientifc truth. This mainly was a reaction against certain forms of excessive post-modernism, relativism and subjectivity. Several authors have discussed these worries to demonstrate that science is unique as a knowledge producing system, that produces robust, reliable and signifcant scientifc knowledge even if we acknowledge that there is no metaphysical, given formal method or rules and foundations to guide us at truth. I will return to that discussion in Chap. 4 when discussing the default of pragmatism for the philosophy of science after the era of the Legend.

For now I want to discuss the reasons for the anxiety and worries academics experience whenever it is publicly discussed that the legendary image of science does not match with the practice behind the doors of the sociology, psychology, philosophy and history departments, but don't make a mistake, behind the doors of laboratories of the natural, biomedical and geosciences as well. This anxiety almost every time pops up also at less public debates about the Legend and how to arrive at a more inclusive way of thinking about science and the design and organisation of our academic institutions. I use the vocabulary frontstage – backstage from a framework developed by Goffman (1959). Thinking about the Legend, our popular image of science, the myth of which has been shattered by its novel criticisers but also by its erstwhile major proponents, Goffman's dramaturgical model for social interactions can be of use. Not only humans in their interactions knowingly assume different behaviour and roles regarding the relationship, interaction and social context they operate in, but likewise public organizations and institutions show different behaviours in different situations, meant for different publics. In many instances in public theatres, formal meetings or media appearances presentations by representatives from fnancial institutes, banks, government or institutes affliated with government, the church, the hospital administration and private companies follow the frontstage narrative or storyline. This, of course, presents the perspective of a reassuring, sophisticated, empathic, politically and socially correct refective organisation. Of course, for different organizations, different items may be considered for an idyllic frontstage story and attitude. It is precisely this function that the Legend has had, and to a still lesser degree still has for science and academia. Most of the writers I cited thus far and will be cited further on, in the introduction and epilogue, but often throughout their analyses in many different wordings relate to the worry they or the scientifc community may have when they debunk the myth of the Legend. The myth of the Legend, as demonstrated above, has been debunked by a few in the 60s, but openly many times since the 1970s by prominent thinkers which has reached a relatively wide audience, outside and inside science. Relatively, since in most cases even during the so-called Science Wars of the 90s when a larger audience got interested in a short while, it is a fairly limited readership. As pointed out above, active natural science researchers or even humanities scholars, in normal times take the Legend for granted, they intuitively know how to produce knowledge and now the mores of their feld, but get nervous when the spell is broken, the myth of the Legend destroyed. All of a sudden one has to realize what the real backstage situation and the correct corresponding narrative is for that. That is very, very hard, since we are coming from the Era of the Legend, where scientifc inquiry as we have seen is held to be unique, timeless, to provide for knowledge with absolute truths and because of its methods, rules and bedrock logical foundations has proven to be successful and to be successfully applied in the modern world. It may have been a problem for the philosophers who gradually saw the Quest for Certainty and their dreams and wonderful philosophies of timeless foundations, unifed science, formal analytic methods, realism and positivity come to an end. For scientist and those working in science and academia the problem is less esoteric and practical but felt to be tricky. The fact that we can no longer use the Legend as a frontstage ideal narrative of science, that has carried much weight since the 1940s, is indeed diffcult. It has been rather effectively used to claim authority for science in public debates, about safety of vaccines, the cause of climate change and what should be done about that. It has been used to discuss many public health and prevention and political issues relating to inequality, fair economics, the regulatory role of government in neoliberal times, but also on an annual basis by some about the absolute prominence of basic natural science.

So, one wonders if we admit that science in the real is done as we do it -producing the claims and insights we believe by a uniquely robust and open, continuous purging, process of testing, of experiments, repeating of experiments, a lot of criticism and debate in a cycle of improving and rejecting- will that convince the public as well as we did convince them with the story of the Legend? Most of the writers, including myself, say yes, that shall do. Be honest, show how knowledge is and has been produced, how robust the process is also when we know that social interests of cultural and personal source are at play. Be frank about the fact that every claim, theory, method, action based on this process is fallible and may eventually be improved, corrected and rejected because it is replaced by a better alternative.

I will here not discuss the Science Wars of the 1990s. '*The One Culture'* by Labinger and Collins (2001) presents a highly readable series of short papers of heavily involved authors with different perspectives on that. The Science Wars was a reaction of the natural science defenders of the Legend to claims in academia thatbecause postmodernist relativism had shown that there is no scientifc method as held by empiricism and positivism- scientifc theories and accepted beliefs are in essence not different from the beliefs derived outside science from superstition and all kinds of popular, religious and personal opinion. This image of science, which derives to be honest in some respects from Rorty's bold interpretation of Willem James' pragmatism, was at the far end of the spectrum opposite of the theory of inquiry of Peirce and Dewey, later extended especially by Putnam (see Chap. 4). The defenders or 'bulldogs' of science went all out with an appeal on the Legend which was not constructive. Fortunately, many philosophers have offered realistic and pragmatic views of science and its practice, without taking refuge to metaphysical and foundational myths of the Legend. I refer to Ian Hacking again, and especially his *The Social Construction of What?* where he in Chaps. 1, 2, 3 and 7 makes a very clear case for the realistic and naturalistic middle ground (Hacking, 1999) and to a very insightful and opiniated review by Shapin (1982). These studies show that there are clearly social and cultural factors at play, but that there are constraints to our claims and ideas in the confrontation with and observation of natural and social reality and these together in a continuous critical debate guide the process of how beliefs get accepted and hypothetical claims become facts. (p33) Our realistic understanding of the practice of scientifc research, where collective reason, experiment and action ground our beliefs which is constrained by conditions in the real world being the natural or the social world.

The good news in my mind is that we can pragmatically make a very good point for the reliability of science as follows. Since modern times we have this new robust collective way of doing science by hypothesizing and experimentation, its everimproving methods, techniques, technologies and the ever-growing collective experience with judgements of claims and experimental results using ever improving sophisticated methods and methods of reasoning. This has resulted indeed in impressive success, changing our lives by changing the unfriendly environment, improving our health and life expectancy, allow quick, convenient and mass transportation, modern communication, increasing personal and global wealth, dealing with issues of energy, and so on. This all has been achieved despite the fact that even in the natural sciences we never had a unifed formal objective value-free scientifc method, an no timeless foundation for our knowledge to build on. Social and political values have always at several levels been involved in our evaluations and criticism of what to study and what to belief in scientifc inquiry. This inclusive deliberation has steered science in society also in modern history to the good but sometimes to the bad. Our common-sense collective methods of inquiry have brought us time and again wonderful results that changed our life's in the past 200 years.

#### **'OMG…….There Is No Foundation!'**

The epistemic core in the philosophy of science and the Legend is empty, was the conclusion of Nowotny et al in their *Re-Thinking Science* that I will discuss in detail in Chap. 5. But I use it here for its analogy with the evolution of the thinking that many of us have had regarding religious beliefs. The story about the Legend of science feels, I image, to many who were raised on the Legend since elementary school, high school and university as loss of certainty and loss of a familiar story that provides for calm and rest of mind. For me it compares to my growing up in a Calvinist family in the North of the Netherlands during the 1960s, where despite the non-academic background of our parents for them and us, reading and studying was part of life. Gradually, I came to realize at the age of 6, I think, that Santa Claus did not exist, but that was alright with me. Much more complicated was in the years between my 14th and 20th year how to think about the origins, foundations and the revelations of our Christian beliefs, ethics and ideal practices. Specially my father was convinced and believed the factual truth of the New Testament, from cover to cover, and this and the ethics and prescribed practices were regularly discussed at home. As a bachelor student I started reading modern theology amongst others Rudolph Bultmann, which made a lasting impression on me. In particular, his demythologization of the biblical texts and his rejection of the supranatural as world views belonging to another cultural context in the past, not appropriate for our modern time were strong images for me. He posed the idea that the biblical stories are not facts but language and texts describing acts of God. There is a core in the text, a message that in every time and culture can have its own narrative form. I had concluded that I did not believe in any of the supernatural, which until now has not caused me more than average anxiety. I was, however, for ever a Calvinist engaged by the ethics and social-democratic politics that came with my upbringing and later reading the modern ethical and political interpretations of the Biblical texts by

(continued)

Bonhoeffer, Sölle, Bloch, Moltmann, and Pannenberg. These writers infuenced Kuitert a Dutch theologian who's public intellectual and emotional struggle I with many others followed since 1971 until his dead in 2017. In a series of books, he goes through a sequence of phases in which he gradually peeled of the layers of classical Calvinist theology and its dogma's. Eventually and it seemed inevitably, he had to admit in the 1980s that there was no foundation, all our speaking and theology about the divine and the supranatural was the product of humans. He was also clear to point out that these revelations thus were not Divine revelations and not God given. Here again the same question as for science comes up, do we have a good enough narrative about Christianity and religion in general if we demythologize its foundation and reduce it to ethics and action in contribution to human fourishing and the good life. Harry Kuitert argued that these 'inspired' ethics and this socialpolitical awareness based on diverse cultural and personal values may shape socialist, conservative or liberal worldviews and policies alike.

# **2.2 Part 2. The Crisis in Analytical Philosophy**

*The spirit of Cartesianism is evidenced not only by rationalists but by all those who subscribe to strong transcendental arguments that presumably show us what is required for scientifc knowledge, as well as those empiricists who have sought for a touchstone of what to count as genuine empirical knowledge.….the frst attack was made by Peirce. Nevertheless it has taken more than hundred years for us to become fully aware of how the Cartesian view distorted the way in which science is actually practiced.'p71* (Bernstein, 1983)*.*

The crisis in analytical philosophy started around 1960 in the philosophical discipline that created the problem in the frst place. Crisis became apparent in open debates when philosophers offcially declared the dead of positivism and empiricism. Philosophers had admitted much earlier that there were already cracks in the idea of a foundation and other aspects of the Legend. C. S. Peirce was on one of the frst *'to attack the Cartesian framework especially in regard to characterizing scientifc knowledge' (p71)* (Bernstein, 1983). His work, in the last decades of the nineteenth century that was followed up by the American Pragmatists James and Dewey until 1940, did not belong to main-stream analytical (logical-empiricist) philosophy and did not get much attention there, apart from Frank Ramsey who's engagement with pragmatism was cut-short and almost forgotten by his untimely dead in 1930 and Nagel, which will be discussed below. Eventually the debate developed with the work of W. V. O. Quine in the 1950s; Popper and Michael Polanyi 1958, 1959; Kuhn in 1962; followed by Toulmin, Feyerabend, Apel and Habermas, Hesse, Hacking, Putnam, and Rorty in the 1970s early 1980s.

This critique on logical positivism and empiricism in the 1970s reached a much larger audience also outside the departments of the philosophy of science. Gradually, it was picked up some active natural scientists or SSH scholars who had an interest in philosophy and sociology of science. However, it appeared -and even in 2021 appears- to be hard for several reasons to go beyond the truly mythical Legend, letting go of the ideas of a timeless foundation and the dreamed formal methods of a science, even when it was realized that it was a method of 'a science that never was'.

Regarding what was at stake, I will again quote Bernstein who has discussed in great detail and transparency these debates and in strong statements the image of science that emerges in the post-empiricist philosophy of science in contrast to image of the logical-empiricists for which Ziman and Kitcher coined the name 'Legend': '*We can interpret this movement of thought as contributing to the demise of Cartesianism that has dominated and infected so much modern thought. The Cartesian dream of hope was that with suffcient ingenuity we could discover, and state clearly and distinctly, what is the quintessence of the scientifc method and that we could specify once and for all what is the meta-framework or are the permanent criteria for evaluating, justifying, or criticizing scientifc hypotheses and theories. The spirit of Cartesianism is evidenced not only by rationalists but by all those who subscribe to strong transcendental arguments that presumably show us what is required for scientifc knowledge, as well as those empiricists who have sought for a touchstone of what to count as genuine empirical knowledge.….the frst attack was made by Peirce. Nevertheless it has taken more than hundred years for us to become fully aware of how the Cartesian view distorted the way in which science is actually practiced.'p71* (Bernstein, 1983)*.*

# *A Detailed History of the Philosophical Demise of the Legend*

As I pointed out at the introduction of this chapter, it is the analysis of the origins and effects of exactly this distortion that is the topic of this book. I will in these remainder of this Chapter discuss the philosophical arguments that convincingly show why the analytical and positivist philosophy failed. I will not go in great detail about the technical discussions. I chose to offer a diverse chronological selection of thoughts and conclusions of the most prominent scholars. I provide the most illuminating citations taken from their work. Readers may wonder why I sometimes cite longer paragraphs. It is because in my opinion they are essential and because I want to give the reader the opportunity to directly read this primary 'material' with no need to have to rely on and trust my paraphrase's and interpretations.

Below I discuss in historical order the work of the major scholars since 1945 the problems of positivism, the analytical philosophy and empiricism, which demonstrates the collective developments in the feld and in some cases the personal development and struggle to break free from foundationalism. For the readers who do not know the authors which I am going to name in the remainder of this chapter, without exception they all were, or are when still alive, the absolute top scholars in their feld. It makes you wonder that only the true elite, the leading scholars in exactly the feld of interest were in a position to challenge the main theoretical ideas and concepts of logical positivism and empiricism, largely the legacy of the Vienna Circle

that had been build up over the past 50 years. Most of them had actually trained with that previous generation of top philosophers who had all contributed and shaped exactly these philosophies. They were mostly students or second-generation students of Wittgenstein in the UK, and Carnap, Reichenbach, Hempel, Quine in the USA. It apparently is quite diffcult, and it requires a reputation and a position of intellectual power to change the thinking in a feld, which is a case in point of Kuhnian paradigmatic revolution and of the power struggle in a 'feld' as described by Bourdieu. (Bourdieu, 1975) Ludwick Fleck, who anticipated Thomas Kuhn's major work by at least 30 years, writing in 1935 about criticism in science said that writers who trained as sociologist or in classics, 'no matter how productive their ideas, commit a characteristic error (Fleck, 1979). They exhibit an *'excessive respect, bordering on pious reverence for scientifc facts'*, cited by Ian Hacking, but Hacking adds: '*The era of excessive respect has passed'* (p60) (Hacking, 1999). I believe that this excessive respect was not so much for 'scientifc facts', but for the mythical power of the scientifc method of positivism that claimed the status of these facts and the status it provided to the scientists.

I start with C. S. Peirce who wrote long before any of them and was part of his own "Metaphysical Club' some 30 years before the Vienna Circle had started (Menand, 2001; Misak, 2013a). Peirce, as said, was later recognised as the *'frst to attack the Cartesian framework'* and infuenced many if not all of major modern philosophers, before 1940 and after some lag time again directly or indirectly since the 1970s (Bernstein, 2010).

C.S. Peirce who did his most infuential writing at the end of the nineteenth century, was one of the frst to attack the Cartesian framework (Bernstein p71). The framework of the idea of a transcendent foundation and the empiricist formal method. He was trained as a chemist in the natural sciences and is now considered to be exceptional regarding his many original ground-breaking contributions to natural science and in particular in the philosophy of science which are studied with renewed interest until this day. Many infuential philosophers have payed tribute to Peirce.

Ernest Nagel in 1939:

*'Peirce's distinctive contributions to logic as the general theory of signs, centre around his pragmatism, his critical commonsensism, and his fallibilism. By far the best known is his pragmatic maxim, proposed as a method for clarifying ideas, eliminating specious problems, and unmasking mystifcation and obscurantism hiding under the cloak of apparent profundity. In one form or another his proposal was adopted by a number of distinguished thinkers, for example, in this country by William James and John Dewey, so that to-day it is almost a common- place. Peirce's own formulation of the pragmatic maxim leaves much to be desired in the way of explicitness and clarity; and more recent formulations, such as those by Professor Carnap and others, have the same general intent but superior precision. I nevertheless venture two general remarks on the Peircean version of pragmatism which, though obvious, merit attention. The pragmatic maxim was intended as a guiding principle of analysis. It was offered to philosophers in order to bring to an end disputes which no observation of facts could settle because they involved terms with no defnite meaning. It was directed at the Cartesian doctrine of clear and distinct ideas, which found the terminus of analysis in vague abstractions claimed to be grasped intuitively, as well as at the common tendency to convert types of behaviours into unknowable agencies controlling the fux*  *of events. Above all, it pointed to the fact that the "meanings" of terms and statements relevant in inquiry consist in their being used in determinate and overt ways. Pragmatism, to employ Peircean language, was thus a proposal to understand general terms in terms of their concrete application, rather than vice-versa. '(bold case by FM)*

*At the risk of treading upon ground on which angels fear to step, I should also like to mention the elementary point that in terms of Peirce's emphasis neither terms nor statements can be regarded as designating, independently of the habits involved in their use. Consequently, "the meaning" of expressions is not to be sought in self-subsisting "facts", "essences", or other "designata", but must be construed in terms of the procedures associated with them in specifc contexts.*

*'Peirce claimed no infallibility for the beliefs of every-day experience, and indeed one of the cardinal tenets of his thought was a universal fallibilism. Peirce's fallibilism is a consequence of his regarding the method of science as the most successful yet devised for achieving stable beliefs and reliable conclusions; it has nothing to do with the malicious scepticism which rejects science on the ground that its conclusions are after all not established as being beyond the possibility of error, only to invoke a special set of imperatives as indubitable objects of human endeavour. Peirce noted that the conclusion of no scientifc inquiry is exempt from revision and correction, that scientists feel surer of their general logic of procedure than of any particular conclusions reached by it, and that the method of science is self-corrective, both as to its own specifc features and the specifc conclusions gained with it.*' Read at the Fifth International Congress for the Unity of Science, Harvard University, September 3–9, 1939. (Nagel, 1940)

Habermas in his *Erkenntnis und Interesse* in 1968 translated in English in 1971 (ref) devoted two chapters to Peirce: *'What separates Peirce from both early and modern positivism is his understanding that the task of methodology is not to clarify the logical structures of our scientifc theories but the logic of the procedure with whose aid we obtain scientifc theories. We term information scientifc if and only if an uncompelled and permanent consensus can be obtained with regard to its validity. This consensus does not have to be defnitive but has to have defnitive agreement as it goal….modern science distinguishes itself by a method of arriving at an uncompelled consensus about our views.'* p91 '*For Peirce there was one method of inquiry, based on deduction, induction and to a small degree inference to the best explanation* (designated abduction by Peirce)*. Truth was roughly, whatever hypothesizing, induction and testing settled down on.'* (p118) Peirce named it the 'scientifc method', the logic of or method of inquiry, but he did not mean to suggest that it is a logical formal system that allows us to get to the truth. Habermas: '*For Peirce this concept of truth is not derivable merely from the logical rules of the process of inquiry, but rather only from the objective life context in which process of inquiry specifable functions: the settlements of opinions, the elimination of uncertainties, and the acquisition of unproblematic beliefs-in short the fxation of belief.' p119* Peirce resolutely rejected the Cartesian foundations, transcendental necessity and conditions, the so-called 'spectator theory of knowledge' that assumes the factvalue dualism. *'For Peirce it is the method'*, says Habermas, '*that takes over the role of an unshakable foundation, the a priori judgements that per defnition cannot be doubted because they are a 'given'*. p97 This thinking of Peirce was many years later followed up by great men like Sellars and Quine. Peirce assumed a constant state not of scepticism but fallibilism, with continuous doubt about our claims in which he anticipated much of Popper's falsifcationism published in 1935.

John Dewey already concluded in the beginning of the twentieth century in many of his writings that philosophy appeared to be an internal debate for philosophers, esoteric and of little value to understanding and guiding the practice of scientifc investigation and its relation to reality, society and human life. Dewey in *The Quest for Certainty* (1933) and elsewhere wrote extensively about what Bernstein called 'the 'Cartesian Anxiety', *the belief of Descartes that the philosopher's quest is to search for an Archimedean point on which we ground our knowledge'*. (1983, p16) I will cite the crisp and concise remarks of Hacking about Dewey's criticism of the philosophy of science of the empiricist and positivistic tradition. Hacking later confessed (Misak, 2007) that he himself found it hard to read Dewey, '*it goes on and on'* and that feeling is familiar to me. Hacking: *'Truth is whatever answers to our present needs, or at least those needs that lie at hand. Dewey gave us the idea that truth is warranted acceptability. The world and our representation of it seems to become at the hands of Dewey very much a social construct. Dewey despised all dualism- mind/matter, theory/practice, thought/action, fact/value. He made fun of the 'spectator theory of knowledge'. He said it resulted from the existence of a leisure class, who thought and wrote philosophy, as opposed to a class of entrepreneurs and workers who had not the time for just looking.*

Hacking, says about Dewey: *'My own view*, *that realism is more a matter of intervention in the world, than of representing it in words and thought, surely owes much to Dewey.'* (p62) (Hacking, 1983). Pragmatism, from Peirce, Dewey, James, Nagel, Quine to Habermas and Hacking, is beyond Cartesian empiricist philosophy and holds that it is this relation to practice, intervention, and actions based on our accepted beliefs that gives value to our beliefs, and not timeless transcendent formal principles that cannot be tested.

Karl Popper (1902–1994), was a most infuential philosopher of science who in his later years also wrote extensively about the open society, freedom and democracy. He was in time and space close to the empiricist positivist philosophers of the Vienna Circle but did however not agree with most of their philosophy. In his "*Logic der Forschung: zur erkenntnisstheorie der modernen naturwissenschaft*" published in 1935, a translation of which appeared in 1959 under the title "*The Logic of Scientifc Discovery*", he criticised the positivist and empiricist philosophy on their major ideas. It has been said that this critique, after the members of the Vienna Circle having tried to incorporate some of it, eventually in the 1950s caused the declaration of the death of logical positivism. Popper wrote in his autobiography, *Unended Quest* (chapter 17), that he rather thought the Vienna Circle came to end because they did not address the real problems, but got immersed in debates about minor problem, puzzles and in particular the meaning of words. Although this echoes the critique on philosophy of Peirce, James and Dewey, they are not mentioned by Popper in this discussion of philosophy of science. Toulmin, but not even Kuhn is mentioned which is remarkable, given the impact of Kuhn's work on the legacy of logical positivists, that was already tangible at the time of Popper's writing (Popper, 1976).

In the 1958 introduction to the English translation of *The Logic of Scientifc Discovery,* Popper states that he is a pluralist and he commends the philosophers *'who do not pledge themselves in advance to any philosophical method, and who make use of epistemology, of the analyses of scientifc problems, theories, and procedures, and, most important, of scientifc discussions. …Its most important representatives… were Kant, Whewell, Mill, Peirce, Duhem, Poincaré, Meyerson, Russel and later in some of his phases Whitehead. Most of those …would agree that scientifc knowledge is the result of the growth of common-sense knowledge. But all of them discovered that scientifc knowledge can be more easily studied. It's very problems are enlargements of the problems of common-sense knowledge. For example it replaces the Humean problem of 'reasonable belief' by the problem of the reasons for accepting or rejecting scientifc theories.'* p22 (Popper, 1959).

Hacking compared Popper's philosophy with that of Carnap's logical positivist philosophy, saying *'They disagreed about much, only because they agreed on basics. It would be nice to have a criterion to distinguish such good science from bad nonsense or ill-formed speculation.*' (p3) Hacking, who wrote that he has been most infuenced in his early days in England by Popper, concludes that despite these differences the positivists and Popper contributed a lot of the timeless image of science The Legend, that ruled before Kuhn, before 1960: *'They thought that the natural sciences are terrifc and that physics is the best. It exemplies rationality and from that they believed in the unity of science.*' p5 (Hacking, 1983).

As I have discussed above, the positivists started with observations from the bottom, building it up into a system of verifed statements about the world. Popper did reject this idea on philosophical logical arguments. In his view it starts top down with hypotheses, that are based on previously obtained knowledge, discussions with peers or simply wild ideas. These conjectures and their contexts determine how we subsequently observe and how we interpret the observations about the world. In Popper's view the claims derived from these observations may after severe experimental testing and discussion between scientists become accepted, held to be 'true'. However, per defnition they are not verifed. On the contrary, theories and their statements are to be regarded falsifable, open to refutation, at any time by further testing and criticism. Poppers 'method' of conjectures and refutations, and his falsifcationism reminds of the 'scientifc method' described by Peirce 50 years before. Like Peirce, Popper completely rejected the idea of the independent, 'given' foundation and the dichotomy between facts and values. Observation, ideas and theory were always entangled. In his thinking, like Peirce, Popper emphasized the power of the method of rigorous and endless testing and of criticism in the community of peers. *"Basic statements are accepted as the result of a decision or agreement, and to that extent they are a convention. The decisions are reached in accordance with a procedure governed by rules'….. 'Thus the real situation is quite different from the naive empiricist. Or the believer in inductive logic.'….'Theory dominates the experimental work from its initial planning up tot the fnishing touches in the laboratory'. (p106)* In a most fascinating metaphor of the 'swamp' he resolutely deals with the issue of the foundation and the 'given'. It is the visualization of this powerful metaphor that I literally never got out of my mind after reading it in August 1975: *'The*

*empirical basis of objective science has thus nothing 'absolute' about it. Science does not rest upon solid bedrock. The bold structure of its theories rises, as it were, above a swamp. It is like a building erected on piles. The piles are driven down from above into the swamp, but not down any natural or 'given' base; and if we stop driving the piles deeper, it is not because we have reached frm ground. We simply stop when we are satisfed that the piles are frm enough to carry the structure, at least for the time being'.* (p109).

In his 1972 Addendum he added*:'1. My term 'basis' has ironical overtones; it is a basis but is not frm. 2. I assume a realist and objectivist point of view: I try to replace perception as 'basis' by critical testing'. Our observational experiences are never beyond testing; they are impregnated with theories. 4. 'Basic statements …are like all language, impregnated with theories'.(p109)* In a later paper, *The Rationality of Scientifc Revolutions,* which takes in to account the community of inquiry and some of the sociological and psychological aspects of the research process, he describes the problems that may arise from this phase of debate and criticism due to the human factor (Popper, 1981) which were discussed in his *Conjectures and Refutations* at length (Popper, 1972).

Willard Van Orman Quine (1908–2000) is everywhere, when you read about the demise of the Legend and about his role, or not, in the resurrection of pragmatism (Misak, 2013b) Quine was familiar to the members of the Vienna Circle but worked whole his life in the USA. In most cases his contribution is very briefy told with short citations. He did not write much, but he made an immense mark through his famous dogma's on empiricism especially by forever rejecting, on analytic logical grounds, thus by using their own weaponry, the analytic–synthetic distinction. This was a blow to the very important yardstick of logical-empiricism and the philosophy of the Vienna Circle (Quine, From a logical point of view, 1956). He demonstrated, or in fact built the argument that the principles of inference that we use to link theory with experience [observations done via our senses] are as Putnam (Putnam, 1981) says [not analytical, nor given or timeless foundations but] '*are just as much subject to revision as any other aspect of our corporate body of knowledge*.' (p30). These rules are thus not 'given', or a priori assumptions but result from our collective thinking, experience and discussion and are such that as Misak phrases: *'everyone would assent to them'* (p200) (Misak, 2013a).

Michael Polanyi wrote in 1959 a short fascinating comment on C.P. Snow's *Two Cultures* that originally appeared in *Encounter*, a monthly Anglo-American journal of politics and culture that did ft Polanyi's political ideas discussed above. This piece is written in the characteristic polemic style of Polanyi who also here puts the issue in a larger political neo-conservative frame, criticizing the hard-boiled scientifc ideals and naturalistic scientism of Bentham and Marx that in his view disrespects truth. '*Our task is not to suppress specialisation of knowledge but to achieve harmony and truth over the whole range of knowledge. This is where I see the trouble. Where a deep-seated disturbance was inherently originally in the liberating impact of modern science on medieval thought and has only later turned pathological'.. 'Science rebelled against authority. It rejected deduction from frst causes in favour of empirical generalisations. Its ultimate ideal was a mechanistic theory of*  *the universe, though in respect man it aimed only at naturalistic explanation of his moral and social responsibilities'. '..scientifc rationalism has been the chief guide towards all the intellectual, moral, and social progress on which the nineteenth century prided itself- and to the great progress achieved since then as well. …Yet it would be easy to show that the principles of scientifc rationalism are strictly speaking nonsensical. No human mind can function without accepting authority, custom and tradition: it must rely on them for the mere use of a language. Empirical induction, strictly applied can yield no knowledge at all and the mechanistic explanation of the universe is a meaningless ideal….because the prediction of all atomic positions in the universe would not answer any question of interest to anybody'. 'Scientifc obscurantism has pervaded our culture and now distorts even science by imposing on it false ideals of exactitude'. (p41)* (Polanyi & Grene, 1969)*.*

Ernest Nagel has been an infuential philosopher, not only through his famous textbook *The Structure of Science: Problems in the Logic of Scientifc Explanation*. (Nagel, 1961) In that pre-Kuhnian seminal work he covered the whole of the philosophy of science of those days, but mostly limited to mainstream analytical philosophy, logical-positivism and empiricism and Popper's philosophy. There is a very short discussion of 'instrumentalism' which refers to American Pragmatism. He was sympathetic to pragmatism as I will discuss later and in his introductory chapter he makes a few remarkable statements which are a critique of the empiricistpositivist philosophy of the 'Legend' that he discusses in the next 300 pages of his book. *'The practice of the scientifc method is the persistent critique of arguments in the light of tried canons for judging the reliability of the procedures by which evidential data are obtained and for assessing the probative force of the evidence on which conclusions are based'. ….'the difference between the cognitive claims of science and common sense which stems from the fact that the former are the products of scientifc method, does not connote that the former are invariably true.'…… 'If the conclusions of science are the products of inquiries conducted in accordance with a defnite policy for obtaining and assessing evidence, the rationale for confdence in those conclusions as warranted must be based on the merits of that policy. It must be admitted that the canons for assessing evidence which defne the policy have, at best, been explicitly codifed only in part, and operate in the main only as intellectual habits manifested by competent investigators in the conduct of their inquiries. But despite this fact the historical record of what has been achieved by this policy ….leaves little room for serious doubt concerning the superiority of the policy….'* (p18)

*'For in point of fact, we do not know whether the unrestrictedly universal (positivistempiricist premises) assumed in the explanation of the empirical sciences are indeed true… .'were this Aristotelian requirement adopted few if any of the explanations given by modern science could be accepted'… 'In practice it would lead to the introduction …that explanations are being judged to have merit by the scientifc* (p43)

Polanyi, who as we saw criticized positivism, concludes two different things from Nagel's account of science: *'Nagel implies that we must save our belief in the truth of scientifc explanations by refraining from asking what they are based upon.*  *Scientifc truth is defned, as that which scientists affrm and believe to be true. Yet this lack of philosophical justifcation has not damaged the public authority of science, but rather increased it'(*Polanyi, 1967*)*

#### **Marxism? Critical Theory?**

Before discussing Kuhn's work and immense impact from the 2020 perspective, I want here from the 1977 perspective refer to another writer who has until this day infuenced my thinking about science, research and society. In September 1976, after a year of philosophy, I had returned to the lab bench to study for my Masters in immunology at the Academic Hospital of the University of Groningen. I continued reading about science and in the Spring 1977 I read Jerom Ravetz's book *'Scientifc Knowledge and its Social Problems'* (Ravetz, 1971)*.* Ravetz (1929-) is a mathematician who became a philosopher of science. After his graduation in the US, he came in the late 1950s to the UK at a time when his even moderate Marxist sympathies were problematic with McCarthyism in the US. In Europe Marxist sympathies in the 1960s and 1970s were not at all a problem in academia and Critical Theory was very much under the infuence of neo-marxist political and social thinking. At university in the early 1970s, there were hard-liners, but one was mostly exposed to Marxism-Light as I would call it. With this I mean, the analyses of socio-economic powers and dynamics, taken out of the Marxist view of inevitable collapse of capitalism and then post-capitalist utopia of the salvation state which had already then not proved realistic in rapidly changing and adapting capitalist economies. However, when re-reading the two collections edited by Rose and Rose from 1976, which I read in 1977, that provide a series of articles on science and society, from an downright Marxist perspective, the Marxist jargon, the mentioning of the blessings of Maoism and the illusion of the end of capitalism and the bourgeoisie is quite weird. Indeed, Stalinism and Leninism and then the Cold War as discussed had blocked these analyses of science and society in the US. Ravetz was most of his professional life affliated with the Centre for Philosophy and History of Science in Leeds where he worked for a short period of time with Toulmin. Ravetz in his book presents a comprehensive analysis of science and research, starting with problems that he expected would become more prominent. He discusses in depth the consequences of what he called 'the industrialization' of science which goes against the Mertonion norms with its protection of property and topdown management. He argued that because of enormous increase in scale, loss of social and ethical control, the system would increasingly face poor quality 'shoddy' research because of the lack of shared value of individual researchers with the scientifc community. On the other hand, he is deeply concerned about the external infuences on the research agenda by powerful private parties, multi-nationals, but also the military and governments. We

(continued)

know noe that Ravetz writing that book at that time was quite visionary. During his whole career he studied issues of uncertainty, risks and unwanted effects attached to the use of novel scientifc knowledge and technology in society (Funtowicz & Ravetz, 1990; Ravetz, 2011). He wrote about the ethics of science and scientists and criticizes the claim 'of neutrality' that was used by researchers to evade their social responsibility. At that early stage preparing for my professional life, reading this book for me was truly a transformative experience and Jerry Ravetz was an inspiration and it was special that he participated when in the late fall of 2012 through 2013 we prepared for the start of *Science in Transition* described in Chap. 3*.*

The huge impact of Thomas Kuhn's *Structure of Scientifc Revolutions,* published in 1962, has already been mentioned many times. It has opened up the debates in the history and sociology of science, but at the same time affected the domain of the philosophers showing through historical and sociological research the problems of logical positivism. Kuhn presented a descriptive account of what scientists do, which sociologically, but also (methodo)logically deviates from the normative positivist scientifc method. He did however not provide judgement about the way science was actually done from the philosophical perspective (positivism) and did not propose an alternative correct formal method. This, in the eyes of his critics, was not logic or if it was logical, they did not agree. They asked the question whether Kuhn's description wasn't in fact normative. They make it, Kuhn writes in discussion with his critics, clear that they don't like his normative prescriptions using terms as *'corrupt our understanding and diminish our pleasure'* and *'a plea for hedonism'*. (Lakatos & Musgrave, 1970) They accuse Kuhn not using logic while they themselves use normative non-cognitive arguments and language. (p237). *'History and social-psychology are not, my critics claim, a proper basis for philosophical conclusions'* (p235). This is an important issue as it points to the gap between the philosophy and the practice of science. *Criticism and the Growth of Knowledge, eds. Lakatos and Musgrave* (Lakatos & Musgrave, 1970) is based on the contributions to a symposium held 13 July 1965 in London. In the fnal chapter, *Refection on my Critics,* Kuhn declares his epistemological viewpoints that are beyond positivism, foundationalism and Popper's theory of falsifcation, but not sceptic nor relativistic. In fact, Kuhn states that his descriptive account of the process of inquiry at the same time indeed is normative. Because, if you want your inquiry to succeed you should use that process, that scientifc method, which of course involves logic, mathematics, statistics and other accepted methods at a given moment in time in a research community. Indeed, science as Kuhn concluded, is a process of the community and not of an individual. A lot of the discussion in *Criticism* in my reading then indeed was about the differences between the descriptive historical and in some respect sociological mode of Kuhn's approach versus the normative mode of especially Popper and to some degree Lakatos. Popper admits that normal science exists, but

fnds it degrading and compares it to applied science and warned for the dangers normal science could pose to science. This is very reminiscent of the elitist scientifc attitudes Snow and Medawar were criticising. Popper even suggested Kuhn did not seem to dislike normal science, whereby he exhibited his normative way, not only of theorizing about science, but also of judging scientists (p52, 53).

I cite some of the most interesting lines of Kuhn:

In the current context of course the question is: who exactly had accepted these canons? Philosophers, but apparently not researchers! In response to Lakatos, Kuhn describes succinctly his conceptual frame:

*'some of the principles deployed in my explanation of science are irreducibly sociological, at least at this time. In particular, confronted with the problem of theory-choice, the structure of my response runs roughly as follows: take a group of the best available people with the most appropriate motivation; train them in some science and in the specialties relevant to the choice at hand; imbue them with the value system, the ideology, current in their discipline (and to a great extent in other scientifc felds as well); and, fnally, let them make the choice. If that technique does not account for scientifc development as we know it, then no other will. There can be no set of rules of choice to dictate desired individual behaviour in the concrete cases that scientists will meet in the course of their careers. Whatever scientifc progress may be, we must account for it by examining the nature of the scientifc group, discovering what is values, what it tolerates, and what it disdains. That position is intrinsically sociological, and, as such, a major retreat from the canons of explanation licensed by traditions which Lakatos labels justifcationism and falsifcationism, both dogmatic, and naïve'. p237, 238.*

It is important to take note that Lakatos, in his one-hundred-page long contribution to this book, wrote that this debate *'did not start with Kuhn. An earlier wave of 'psychologism' followed the breakdown of justifcationism. For many, justifcationism represented the only possible form of rationality: the end of justifcationism meant the end of rationality …………After the collapse of Newtonian physics, Popper elaborated new, non-justifcationist critical standards. Finding them untenable, they identify the collapse of Popper's naïve falsifcationism with the end of rationality self*.' P178. Lakatos, a true Popperian and believer in the 'scientifc method' at that time, started to work on his concept of Research Programmes, a mix of Popperian and Kuhnian thought.

In the remainder of the chapter, Kuhn responds to the critique that his description of science, without a rejection of the methods used, opens the doors to relativity and nihilism. It was argued that personal opinion, mob psychology and elites with power and vested professional interests could determine the outcome of discussions regarding theory choice. He cites the non-cognitive, but important criteria and values that are being used and accepted in communities of inquirers and have been implied by Popper in his normative description of theory choice, including '*accuracy, scope, simplicity, fruitfulness'*. (P261, 262) Kuhn emphasizes that these are not rules that can be applied in a straightforward manner and his historical research has shown that they may evolve and change over time in the community.

When Kuhn prepared his book, in the late 1950s, logical positivism despite the prominent works by Quine and Sellars, still ruled in the philosophy of science and pragmatism was not considered to be a sound and fruitful alternative. Many still believed that the problems of positivism could be solved by analytical philosophy. But Kuhn's analyses and conclusions as expressed above are, although not cited by him, reminiscent of American pragmatism and the critiques of Peirce and Dewey on the dominant philosophy of science of their times.

John Ziman (1925–2005) was a physicist who between 1960 and 2000 was one of the frst to write systematically, in depth and broadly about science. In 1968 he published *Public Knowledge* (Ziman, 1968) his frst of nine books on science and as Jerome Ravetz, Ziman's contemporary colleague and science writer, in his obituary wrote: *'In this he bypassed the debates among the philosophers who saw science as a collection of "theories" requiring some sort of logical proof; for him the essential feature of scientifc knowledge is its social character.'* (Jerry Ravetz, Guardian, February 2005).

#### **It's Anthropology, Stupid!**

In most of their books, Toulmin, Hanson, Ravetz and Ziman, but also Polanyi, take all aspects of the scientifc enterprise into account in their analyses of how consensus regarding reliable knowledge is produced and thus what distinguishes science as a social activity. In their opinion it is exactly the complex of the methods, personal psychology, the community and the sociology of the researchers in organizations that determines what science is. Their writings went against the widely held believes about science and as a consequence were virtually neglected by main-stream philosophy, history and sociology. Because of its multidisciplinarity, in addition their work did not belong to one of these classical academic disciplines. Similarly, even Bruno Latour in his *We were never Modern* complained about the slow recognition of Latour and Woolgar's *Laboratory Life* by philosophers and sociologist of science*.* (Latour, 1993; Latour & Woolgar, 1979) This was duly confrmed by Hacking in his very late 1988 (!) review of '*Laboratory Life'*. With regard to this seminal book of 1979 and his own 1983 book that I here cite a lot and wherein he argues to take a look at the practice of science, he declares that *'it was shameful not to examine the one outstanding piece of work then available that took laboratory science seriously and argued the strong anti-realist doctrine in existence'*.(p278) (Hacking, 1988) Latour pointed out that we do accept anthropology crossing all these academic territories, but apparently we do not allow this for an anthropology of the tribe of humanity that is involved in science.

This may, Ravetz believed, be the reason that this type of work has had relatively little impact (Ravetz, personal communication 2013). That may well be the case, but as argued above, meta-science research drew in general very little attention from those active in research in the academic disciplines or in the 'corridors of power' of academia (Miedema, 2012). Lack of impact has also been blamed on the fact that the work of these authors lacked a novel theory, theoretical frame or a specifc novel concept. Exceptions to this are Polanyi's concept of tacit knowledge and Toulmin's metaphor of maps for theories (1953) and his evolutionary concept of progress in science (1972). I disagree with this critique, as I my opinion the main hypothesis for which they provided evidence and which is the basis for this book, is that in the history of science, the dominant image of science which proved philosophically wrong around 1960, was strongly politically and culturally determined and has until now distorted and hurt the practice of science in many different ways. It is on the basis of these insights, that many scholars have since then began to study the practice of science. These studies in the recent past have resulted in renewed movements to improve the practice of science and make it more suitable to contribute to solve the grand challenges of the twenty-frst century. John Ziman already in his early books *Public Knowledge* and *Reliable Knowledge* has provided insights from the trenches of science about the problem of the myth of the 'scientifc method', which at that time still few others understood and for which Ziman later coined the term 'the Legend' (Ziman, 2000). He wondered in 1968 (!) (Ziman, 1968) how this *'logicoinductive' metaphysics of Science.. can be correct, when few scientists are interested in (it) or understand it, and no one ever uses it explicitly in his work? But if Science is not distinguished from other intellectual disciplines neither by a particular style or argument nor by a defnable subject matter, what is it?* (p8). He then sketches the social process of inquiry, hypothesis, testing and criticism and states that '*it is not a subsidiary consequence of the 'Scientifc Method'; it is the scientifc method itself*.''*The defect of the conventional philosophical approach to Science is that it considers only two terms in the equation. The scientist is seen as an individual, pursuing a somewhat onesided dialogue with taciturn Nature. But it is not like that all. The scientifc enterprise is corporate. It is never one individual that goes through all steps of the logico-inductive chain; it is a group of individuals, dividing their labour but continuously and jealously checking each other's contributions'*. (p9)

John Ziman could in those days, fnd virtually no literature on consensus building by the community and the social process and *'that makes the Philosophy of Science nowadays so arid and repulsive. To read the latest volume on this topic is to be reminded of the Talmud…' It is fercely professional and technical and almost meaningless to the ordinary working scientist. This is unfortunate ..I shall try to heal the breach by talking semi-philosophically about the intellectual procedures of scientifc investigation.'* (p31).

In *Reliable Knowledge*: *an exploration of the grounds for belief in science (J. M.* Ziman, 1978*)* an important book in this context, Ziman did the same bypass as in *Public Knowledge* as in all his books regarding the philosophical basis of the Legend. In the introductory paragraph 1.4 he frmly states that from data, diagrams, models or pictures, '*meaning cannot be deduced by formal mathematical or logical manipulation. For this reason scientifc knowledge is not so much 'objective' as 'intersubjective' and can only be validated and translated into action by intervention of human minds' (*p7). Ziman is very realistic and knows the daily practice of physics and does not conceal weaknesses known to investigators but disguised by the believers of the Legend: *'The achievements of intersubjective agreement is seldom logically rigorous; there is a natural psychological tendency for each individual to go along with the crowd, and to cling to a preciously successful paradigm in the face of contrary evidence. Scientifc knowledge thus contains many fallacies, mistaken beliefs that are held and maintained collectively and which can only be dislodged by strong persuasive events*.' (p8.) He describes how scientist are 'brainwashed' during their training in the concept, accepted beliefs and methods in the current paradigms of their feld. He explains in great detail and nuance how in the 'social model of science', the scientifc community produces the knowledge we designate as scientifc knowledge and what makes it unique and reliable. Ziman builds further on the work of those who criticised positivism and the Legend - Polanyi, Hanson, Toulmin and Kuhn- published in the decade before. Ziman points to fact that there is not one scientifc method, there are many dimensions to scientifc knowledge and *'that explains the strange sense of unreality that scientist feel when they read books about the philosophy of science' (p84)*. From this point of view from the natural sciences, he concludes that the social sciences and humanities of course can produce reliable scientifc knowledge and he states in an unexpected humanistic lyric paragraph *that 'the challenge to the behavioural sciences is not coming from physics but from the humanities'*. (p185).

Jerome Ravetz in his, in the STS felds well-known, *Scientifc Knowledge and its Social Problems* presented a unique philosophical-sociological analysis. (Ravetz, 1971) It provides an integrated very rich view of science, its theoretical assumptions, its ideologies, power games, issues of ethics and social responsibilities and the sociology and politics of the system and the interaction with society. Ravetz cites a broad body of the most relevant scholars at that time. He refers frequently to the work of his temporaries Toulmin, Ziman, Rose and Rose and especially Polanyi's '*Personal Knowledge'* (Polanyi, 1958, 1962)*.* He really 'took a look' at the practice of science and especially emphasizes science as craftmanship and subsequently discusses the philosophical assumptions about the special status of theories and how knowledge is produced. He, on the basis of his understanding how science and research is being done, rejects the positivist and foundationalist ideas With respect to 'the scientifc method' and positivism he clearly states that in research the underlying '*principles and precepts that are social in their origin and transmission, without which no scientifc work can be done.. guide and control the work of scientifc inquiry.'* (p146) More explicitly: *'The individual scientist; and the criteria of adequacy are set by his scientifc community, not by Nature itself.*' (p149) With respect to *'the maturity of a feld an important part lies in the strengthening of the criteria of adequacy. This is not all of course; the development of new tools, and the creation of an appropriate social environment are equally important. Nor can the strengthening of criteria of adequacy be done in an abstract, automatic fashion, as by attempted imitation of a succesful feld* (p157). About the relation between philosophy and the practice of science he says: *'Philosophers of science have attempted, with some success to provide a rationale for the different basic patterns of argument, showing why it is reasonable for an intelligent person to place reliance on them….But as these philosophical arguments become more refned and sophisticated, they drift further and further from the practice of science.*' Finally, for the present discussion it is of interest to close with the following citation on the dichotomy of values and facts. Ravetz, unlike Polanyi, but like Bernal whom he also personally knew, sees research primary as a social activity that needs conscious strategies to be able to make proper judgements regarding problem choice. He explicitly mentioned values other than strict cognitive arguments that have to enter into these evaluations (p161). '*The criteria of value, and judgements based upon them, form an interesting contrast to those of adequacy. …we shall fnd ourselves involved in problems of the social activity of science. …The exclusion of problems*

*of value from the traditional philosophy of science has its roots in the ideology of modern natural science as it was formed through many generations of struggles….. the considerations of social value by which all other human activities are assessed were declared irrelevant'* p160.

Mary Hesse (1924–2016) studied mathematics, physics and philosophy and taught mathematics and philosophy at several universities in England. She has written extensively on the philosophy of science. Mary Hesse wrote in 1972: *'During the last half-century much of professional Anglo-American philosophy of science has been devoted to detailed development of internal logic of natural science based on empiricist criteria, and also on attempts to show how this logic applies also in the social sciences and in the study of history. Suggestions….to the effect that there are other modes of knowledge than the empiricist were sometimes actively resisted but more usually totally disregarded'. 'It was held that adoption of at least a modifcation this empiricist method is required for human sciences 'to attain knowledge status at all' which in her view is 'imperialism claimed for natural science'* (p27) (Hesse, 1972).

*'These distinctions that I believe are made largely untenable by recent more accurate analyses of natural science.*

*'Let us however concentrate for a moment on the natural science half of the dichotomy what is immediately striking about it to readers versed in recent literature in philosophy of science is that almost every point made about the human sciences has recently been made about the natural sciences. And that the fve points made about the natural sciences presuppose a traditional empiricist view of the natural science that is almost universally discredited'* (p277) (Hesse, 1972)

Richard Rorty's *Philosophy and the Mirror of Nature* published in 1979 had enormous and immediate impact and for most scholars of pragmatism was the start of the pragmatic turn (Rorty, 1979). Rorty, in chapters III and IV, starts by discussing in depth the serious critiques of Quine and Sellars on the classical dichotomies of logical positivism. In addition, he took the pragmatic turn in chapter VII discussing at length Kuhn's work and putting it frmly in the larger context of the pragmatism of John Dewey. He concludes that 'analytic' epistemology (i.e. "philosophy of science") became increasingly historicist and decreasingly "logical" (as in Hanson, Kuhn, Harré and Hesse) (p168). He discusses the 'behavioristic' critiques of Quine and Sellars, following Wittgenstein's *Philosophical Investigation*s published at the same time in 1953, on *'the two distinctions the "given" and "that what is added by the mind" and that between the "contingent" (because infuenced by what is given) and the "necessary" because entirely "within" the mind and under its control)…he presents them as forms of holism. As long as knowledge is conceived of as accurate representing- as Mirror of Nature- Quine's and Sellar's holistic doctrines sound pointlessly paradoxical, because such accuracy requires a theory of privileged representations, ones which are automatically and intrinsically accurate. …I shall be arguing that their holism is a product of their commitment to the thesis that justifcation is not a matter of a special relation between ideas (or words) but of conversation, of social practice. …we understand knowledge when we understand the social justifcation of belief, and thus have no need to view it as accuracy of representation.'(p170)…*this is, Rorty says, '*the essence of what I shall call epistemological behaviorism, an attitude common to Dewey and Wittgenstein'. (p174) 'Epistemological behaviorism (which might be called "pragmatism" were this term not a bit overladen)…is the claim that philosophy will have no more to offer* t*han common sense (supplemented by biology, history, etc) about knowledge and truth. (p176)*. The term 'behavioristic' may seem peculiar, but refers to the social process by which a community of inquirers come to produce and accept knowledge and beliefs.

In the pages that follow Rorty dispenses with foundationalism and even with philosophy at large, the latter goes much too far for philosophers like Kitcher, who see enough problems to philosophize about. Indeed, since the demise of the Legend, there is no systematic 'grand unifed theory' in the philosophy of knowledge. As I will argue in Chap. 4, pragmatism has a lot to offer with regard to our understanding and philosophizing about knowledge and knowledge production. As Rorty discussed (p367), it may not provide a systematic alternative, but it does provide a hermeneutical method and viewpoint about science and inquiry (see also Kuhn The essential tension p xiii and xv). This, to many a philosopher of the analytic tradition may have been disappointing and the main reason to not take pragmatism serious as philosophy, but must be understood in that pragmatism is a reaction by 'peripheral' philosophers (James, Dewey, Wittgenstein, Heidegger) to a 'systematic' philosophy which Rorty designates a mainstream analytic 'superstition'. These 'peripheral' philosophers are according to Rorty the 'edifying' philosophers. They do not provide a system with a set of rules but offer moral and intellectual instructions and enlightenment.

As Flyvberg (2001) argues, hermeneutics is not only relevant for the social sciences but also for the natural sciences '*as it is now argued that natural sciences are historically conditioned and require hermeneutic interpretation. Natural scientist, too, must determine what constitutes relevant facts, methods, and theories; for example, what would count as "nature".* (p28).

Nancy Cartwright, a mathematician and philosopher who has studied the practice of physic in relation to the myths of analytical philosophy. She wrote *The Dappled World* (Cartwright, 1999) in follow up of *How the Laws of Physics Lie* (Cartwright, 1983)*,* in which she discusses the classical ideas of the unity of science and the myth of the universality of physics and she takes for comparison economics, the discipline that is famous for imitating (or since the fnancial crisis having imitated?) physics. The physics that never was, as Cartwright shows. *The Dappled World* is a very technical book, but its conclusions (p9 and 10) are clear theories and claims have been stablished in very artifcial settings in the laboratory or as in economics by keeping everything else the same (*ceteris paribus*) both which in the real world are rare to occur: *'I conclude that even our best theories are severely limited in their scope. For, to all appearances, not many of the situations that occur naturally in our world fall under the concepts of these theories…..''The logic of the realist's claim is two-edged: if it is the impressive empirical successes of our premier scientifc theories that are supposed to argue for their 'truth'…then it is the theories as used to generate these empirical successes that we are justifed in endorsing. How do we use theory to understand and manipulate concrete things- to model particular physical or socio-economic systems? The core idea is … the belief in one great scientifc system, a system of a small set of well-co-ordinated frst principles admitting a simple and elegant formulation, from which everything that occurs, or everything of a certain type or in a certain category that occurs, can be derived. But treatments of real systems are not deductive, ….(not) even if we tailor our systems as much as possible to ft our theories, which is what we do when we want to get the best predictions possible.'*

This is the reason, and that is well known, why many drugs shown to have benefcial effects in a highly selected patient population and well-controlled clinical trials, don't do as well in clinical practice. Cartwright got a lot of criticism to the kind of criticism she articulated in *How the Laws of Physics Lie* but her response is clear, and relates to the myth of the Legend: *'I agree that my illustrations ….are 'a far cry' from showing that the system must be a great scientifc lie. But I think we must approach natural science with at least as much of the scientifc attitude as natural religion demands'.*

Her examples are from physics, economics, medicine and genetics. Her conclusions reminds on the one hand of the arguments of Nagel discussed above, and on the other hand of the persuasive work of Richard Lewontin, which in a less analytic and technical way, criticizing the ideologies of biology, genetics, molecular biology and the dream of the human genome project and thus of the positivist molecularbiologists and clinicians-researchers who believed would reductionist science solve the problem of our diseases- cancer, cardiovascular, and mental illnesses alike. (Lewontin, 2000; Lewontin et al., 1984).

Hillary Putnam (1926–2016) was a mathematician and philosopher who has had a broad and deep impact on mathematics, ethics and the philosophy of science. He is famous and admired for his critical thinking about the work of others, and interestingly, as well as about his own work and has as consequence changed his philosophical ideas and positions several times in his long career. He started as a student with Hans Reichenbach, a major fgure in pre-war analytical philosophy. Via positions amongst others at Princeton and MIT he worked at Harvard until 2000. In his later years he wrote widely about American pragmatism (Putnam, 1995; Putnam & Conant, 1994) and in particular how it could overcome the problems of the analytical philosophical tradition including foundationalism, and the various dualisms such as the analytic-synthetic, the objective-subjective and the fact-value dichotomies. His *Reason, Truth and History* (Putnam, 1981) is illuminating with respect to the faws of the positivist philosophy of the Legend. In particular Chap. 3, but also more broadly the thinking presented in Chap. 8 are insightful. In 2004 he published *The collapse of the Fact/Value dichotomy* (Putnam, 2002) where he discusses how most 'analytical philosophy of language and much metaphysics and epistemology has been openly hostile to talk of human fourishing, regarding such talk as hopelessly "subjective"- often relegating all of ethics, in fact, to that waste baker category' (p viii), and he argues for the economics approach of Amartya Sen. He delves deep, as always, and I will leave that to the more experienced reader but here I cite the very last paragraph which is in plain English but boldly worded which makes his position after a lifetime hard work on exactly these matters very clear:

*'I have argued that even when the judgments of reasonableness are left tacit, such judgments are presupposed by scientifc inquiry (indeed, judgments of coherence are essential even at the observational level: we have to decide which observations to trust, which scientists to trust-sometimes even which of our memories to trust.) I have argued that judgments of reasonableness can be objective, and I have argued that they have all of the typical properties of value judgments. In short, I have argued that my pragmatist teachers were right: "knowledge of facts presupposes knowledge of values." But the history of the philosophy of science in the last half century has largely been a history of attempts - some of which would be amusing, if the suspicion of the very idea of justifying a value judgment that underlies them were not so serious in its implications- to evade this issue. Apparently any fantasy -the fantasy of doing science using only deductive logic (Popper), the fantasy of vindicating induction deductively (Reichenbach), the fantasy of reducing science to a simple sampling algorithm (Carnap), the fantasy of selecting theories given a mysteriously available set of "true observation conditionals," or, alternatively "settling for psychology" (both Quine)- is regarded as preferable to rethinking the whole dogma (the last dogma of empiricism?) that facts are objective and values are subjective and "never the twain shall meet." That rethinking is what pragmatists have been calling for for over a century When will we stop evading the issue* ("knowledge of facts presupposes knowledge of values.") (insert FM) *and give the pragmatist challenge the serious attention it deserves?* (p145)

I have in this philosophical time-travelling now arrived in the twenty-frst century. I want to discuss Philip Kitcher's work, which for several reasons is of interest in this context. Starting like Putnam from the analytical science tradition, he has described his intellectual history since the 1980s, in the beginning criticizing some and defending other parts of the Legend but gradually losing faith. Kitcher has been refecting on the philosophical transition he went through, from empirical positivism, natural empirism to a form of neopragmatism. Even in times when the more general pragmatic turn was already going on in the feld (Bernstein, 2010; Putnam & Conant, 1990), he experienced how different this philosophical approach was, not in the least in the eyes of his mainstream analytically thinking peers (Kitcher, 2012). Kitcher in 1999 was appointed as John Dewey Professor of philosophy at Columbia. From his website: '*Following Dewey, I believe in the need for a reconstruction of philosophy (so that it will not be a "sentimental indulgence for the few"), and I worry about the increasing narrowness and professionalization of academic philosophy. In working with graduate students, I hope to instil a capacity for clarity and rigor without sacrifcing the sense of why philosophy matters.'*

In his *The Advancement of Science* (Kitcher, 1993), which carries the strong subtitle "*Science without a Legend, Objectivity without Illusion',* this struggle is throughout the book most visible, but Kitcher is to be recommended for being very explicit about it upfront and in the epilogue: '*Once, in those dear dead days, almost, but not quite, beyond recall, there was a view of science that commanded wide spread popular and academic assent'….'Legend celebrates scientists as well as science'. …..scientists have achieved so much through the use of the SCIENTIFIC METHOD.'..'there are objective canons of evaluation of scientifc claims; by and large, scientists (at least since the seventeenth century) have been tacitly aware of these canons and have applied them in assessing novel or controversial ideas….' (*p3).

'*So much for the dear dead days. Since the late 1950s the mists have begun to fall. Legend's lustre is dimmed. While it may continue to fgure in textbooks and journalistic expositions, numerous intelligent critics now view Legend as a smug, uninformed, unhistorical, and analytically shallow. Some of the critiques, science bashers, regard the failure of science to live up to Legend's advertising as reason enough to question the hegemony of science in contemporary society. I shall not be concerned with them, but with the critiques of the Legend bashers, those who believe that Legend offered an unreal image of a worthy enterprise.'*(p5) Kitcher acknowledges that although he believes that the classical philosophy *'belongs amongst the greatest accomplishments of philosophy of our century'*, it has been shown to have its problems. He only once in a footnote (!) (p7) cites the devasting critique of Popper discussed above and admits that '*despite efforts of a few philosophers, little headway has been made in fnding a successor for Legend. If anything, recent work in the history of science and the sociology of science has offered eve more sweeping versions of the original critiques'……, I am not yet ready to abandon the search for generality'* (bold applied by FM) p8.

Kitcher is much concerned with the objectivity of theory choice where indeed (social) criteria are at play which according to Legend are non-epistemic because external. He also wrestles many pages with the classical problem of representation of reality by theory and of realism of the objects of science and in these discussions uses, as per Legend, the success of natural science as kind of foundation, a warranty for objectivity and realism. This feels like causality reversed. Kitcher at that time believed that Legend could philosophically and sociologically be rescued, in his way or another. He believed that *'the Legend was broadly right about the characteristics of science. Flawed people, working in complex social environments, moved by all kind of interests, have collectively achieved a vision of parts of nature that is broadly progressive and rests on arguments meeting standards that have been refned and improved over centuries. Legend does not require burial but metamorphosis.' p390* This defence of Legend is remarkable since writing this in 1993, he is aware and discusses the seminal work of the scholars who convincingly showed, as I discussed above, that the myth of 'the scientifc method' and its normative canons, never did relate much to daily practice of inquiry and the idea of foundationalism did not hold. Kitcher (p10) admits that the Legend was a normative construction, but incorrectly seems to suggest it came from studying science and can be rescued by studying the practice of science again. Kitcher was at that time critized by Shapin (cited by Kitcher p303) that he still worked from the Legend's 'individualism' of the scientist instead taking the work of many scholars to heart that shows the social process and the community of inquiry in practice. Very interestingly, in the fnal pages he suggests that philosophy should be normative and could suggest ethics and values for how the enterprise of science could (and should) be organized to optimally contribute to human fourishing: '*Yet even if the metamorphosis of Legend attempted here clears away those errors, it does not address the issue of the value of science. To claim as I have done that that the sciences achieve certain epistemic goals that we rightly prize is not enough- for the practice of science might be disadvantageous to human well-being in more direct was, practical ways. A convincing account of practical progress will depend ultimately on articulating an ideal of human fourishing against which we can appraise various strategies for doing science. Given an ideal of human fourishing, how should we pursue our collective investigation of nature……..how should we modify the institution as to enhance human well-being?…. The philosophers have (no the Legend has .., FM) ignored the social context of science. The point however is to change it."* (p391) I will return to the later work of Kitcher, which shows his sharp pragmatic turn, when this topic is discussed further in Chap. 4.

Helen Longino (born 1944) has focussed throughout her career as philosopher on the social character of scientifc inquiry. She is motivated in this work by Women's Studies, the role of social values and criteria, equality, gender and inclusiveness. She has studied it from different theoretical and practical viewpoints. She understands the Legend and the struggle of the classical philosophers, including Kitcher, to break free from the classical view of the scientifc method, the Legend. She is avoiding the extreme, that there is no objectivity in scientifc inquiry at all, argued by those who claim that it is determined by values and interests only and unconstrained by empirical observations. In her widely appreciated *'Science and Social Knowledge'*(Longino, 1990) her tour the force on this is described for the frst time in an analysis contrasting the logical positivist

philosophy of Hempel with the 'Wholism', as she calles it, of Hanson, Kuhn and Feyerabend. She goes basically through the same intellectual moves as the writers cited above and, in the end, tries to present a contextual empiricist 'scientifc method' that is truly social in which the community of inquirers also takes social values pertinent to the context of the work into account. '*My concern is that with a scientifc practice perceived as having true or representative accounts of its subject matter as a primary goal or good. When we are troubled about the role of contextual values or value-laden assumptions in science, it is because we are thinking of scientifc inquiry as an activity whose intended outcome is the accurate understanding of whatever structures and processes are being investigated. If that understanding is itself conditioned by ours or others' values, it cannot serve as a neutral and independent guide.*' Against this she argues: *'The dichotomy of these approaches should not be seen so much as a contraction to be resolved in favour of one or the other position, so much as refective of a tension within science itself between its knowledge-extending mission* (application in contexts*) and its critical mission* (better theories)' p34.

*'In assessing particular research programmes*, *it is important to keep in mind that knowledge extension* (testing the effects of claims in experimental and real-world settings) *and truth* (as accepted beliefs, Longino must mean to say) *can guide scientifc inquiry and serves as fundamental, but not necessarily compatible, values determining its assessment.' Thus, while a demonstration of the contextual value ladeness of a particular research program may serve to disqualify it as a source of unvarnished truth about its subject matter, such demonstration may have little bearing on one's assessment of it as an example of scientifc inquiry.'(p36) (*non-italic inserts are mine).

There is in Longino's method, her epistemology, no timeless foundation, but there are background assumptions, ethical, political, social and other, and there is a practice of reasoning about them. They are under scrutiny, with full criticism and eventual acceptance by the community of inquirers thus correcting for subjective individual preferences (p216). These assumptions, like the classical scientifc methods, are not insensitive to cultural and political changes brought about over periods of time by changes in the world views of citizens wherever they live their life. The myth or the Legend, Longino correctly observed, has served as a timeless and stabile disguise providing an account that can *'render invisible the background assumptions. The methodologies associated with logical positivism did render them invisible, which is, I suspect, one reason they remain persuasive among scientists even after being abandoned by philosophers……The myth of value neutrality, that is the consequence of the more general view that scientifc inquiry is independent of its social context, is thus a functional myth.' (p225).*

This is an important insight. In fact, by employing this myth of neutrality, scientifc inquiry and science as a knowledge system in society is in frst instance mainly conservative, resisting critique regarding its accepted theoretical core, and its refection on its own societal activity. It prohibits, or at least discourages on methodological (epistemic) grounds, also the critique through scientifc inquiry of the institutions and social developments and conceals the interaction of science with public and private power structures in society. This is as an example refected in the negative response of Polanyi and Russell, key opinion leaders in UK physics on BBC radio broadcasted the beginning of 1945, to a caller's question if something of practical use could be expected to be done with quantum physics. Much later in 1962 Polanyi *'actually," admits, "the technical application of relativity…was to be revealed within a few months by the explosion of the frst atomic bomb."* 'Polanyi *argued that because science is unpredictable, then its subsequent technical and social outcomes are even more so. He weaves an intricate analogy between the conduct of science and the play of the economic market, both of which exemplify how individuals can maximize socially benefcial outcomes by pursuing their own interests and adjusting, mutually but independently, to the interests of others. The same "invisible hand" that guides the market guides science. While he allows that "Russell and I should have done better in foreseeing these applications of relativity in January 1945," he extends their own incapacity back a half century by also arguing that "Einstein could not possibly take these future consequences into account when he started on the problem which led to the discovery of relativity" because "another dozen or more discoveries had yet to be made before relativity could be combined with them to yield the technical progress which opened the atomic age" (*Cited in (Guston, 2012) Guston 2012 Minerva). A bit dubious this evasion of one of the major ethical and political issues of twentieth century science, since Einstein and Szilard having fed the Nazi's to the US, in 1939 urged Roosevelt to get an atomic bomb build before Hitler did. Its deployment against Japan had not been the idea of a pacifst Einstein and many involved scientists, they instead had seen it as a major means of deterrent. Einstein was until his dead active in the Federation of Atomic Scientists and the Pughwash Conferences against proliferation of nuclear arms.

Longino concludes that this myth of neutrality is detrimental to major aspects of the practice of modern science in chapters on research on sex differences, and the genetics and biology of behaviour where 'hard' data is interpreted based on uncontested hidden social assumptions. Inquiry explicitly investigation and criticizing these cultural assumptions is per Legend declared non-scientifc though, because of contextual assumptions that are made explicit.

Ten years after, in *'The Fate of Knowledge'* (Longino, 2002) she has gone further down the road, further away from the timeless certainty of the Legend. She writes: *'My aim in this book is the development of an account of scientifc knowledge that is responsive to the normative uses of the word "knowledge" and to the social conditions in which scientifc knowledge is produced. Recent work in history, philosophy, and social and cultural studies of science has emphasized one or the other. As a consequence, accounts intended to explicate the normative dimensions of our concept- that is elaborating the relation of knowledge to concepts such as truth and falsity, opinion, reason, and justifcation- have failed to get a purchase on actual science, whereas accounts detailing actual episodes of scientifc inquiry have suggested that our ordinary normative concepts have no relevance to science or that science fails the test of good epistemic practice. That can't be right. The chapters that follow offer a diagnosis of this stalemate and an alternative account. I argue that the stalemate is produced by an acceptance by both parties of a dichotomous understanding of the rational and the social.*' (p1).

This is one of the main problems in science and academia, nearly 20 years later because we still see this stalemate and in our debate about science its characteristic discourse. Longino addresses the underlying assumption of this classical dualism of the Legend and rejects them, which opens up the possibility of a concept of science where internal and external criteria of value both can be used to make choices in science. She in 2002 immediately (on p3) goes to the work of Mill, Peirce and Popper who early on realised that science and the method used to come to accepted beliefs is not an individual but a truly social process, which as we have discussed goes against the Legend. Regarding Popper she points out correctly that Popper, as cited above, praised philosophers who involve in their analyses '*theories, and procedures, and, most important, (of) scientifc discussions', 'contingent factors operating in the world of human affairs are beyond his epistemology*'. '*Unlike discussions by Mill and Peirce, Popper's theory of knowledge deliberately bypasses the connection to science and inquiry as practiced and remains the ideal'* (p7). I cite her own resume of the book which is mainly dealing with the problem of what she calls the Rational-Social Dichotomy which as we saw is a main pillar of the Legend: *'The work in social and cultural studies has stimulated a range of responses from philosophers. Some simply rejected the relevance of this work to philosophical concerns, or ….have seen it as empirically and conceptually misguided. Some like Philip Kitcher…have tried to take the sting out of it, by sifting through the claims of the sociologists and sociologically oriented historians attempting refutation of those they deem extremist, and then incorporating a sensitivity to history or sociological analysis into their constructivist accounts of inquiry. …, I argue that these efforts, too, are vitiated* by *a commitment to the dichotomy of rational and the social. I offer an account of scientifc knowledge that not only avoids the dichotomy but integrates the conceptual and normative concerns of philosophers with the descriptive work of the sociologists and historians.*

Longino aims to integrate in the understanding of scientifc inquiry the fact that '*cognitive capacities are exercised socially, that is interactively'* and argues that more '*more complete epistemology for science must include norms that apply to practices of communities in addition to norms conceived as applying to practices of individuals. Following through on the consequences of the analyses breaking with conventional views of scientifc knowledge as permanent, as ideally complete, and as unifed and unifable….means accepting provisionality, partiality, and plurality of scientifc knowledge. ...I insist on an epistemology for living science, produced by real empirical subjects. This is an epistemology that accepts that scientifc knowledge cannot be fully understood apart from its deployments in particular material, intellectual and social contexts*.' She makes it clear that there need to be pluralism in these epistemologies.

Longino wants to take advantage in her epistemologies of both the Rational and the Social and takes us through some technical chapters, in which she makes it clear that we have a lot to fgure out if we (want to properly) use a mix of rational normative criteria from the philosophers and the social criteria and norms the sociologists have revealed. This is especially interesting knowing that scientists do use in their feld validated standard, methods and accepted ways of reasoning, but do not take the normative canons of the Legend to seriously in their daily practice, whereas they use consciously and unconsciously the social norms and values derived from their cultural upbringing in all its aspects of a society. In the last ten pages she concludes that the Rational-Social classes of criteria and norms are thus not used in separation, *'sociality does not come into play at the limit of or instead of the cognitive. Instead, these social processes are cognitive. ….and the social epidemiologist must have resources for the correction of ..epistemically undermining possibilities.'* This is required since opening up to the social, the stakeholders in society, opens up to power games which may be to the disadvantage of those problems which are vulnerable to 'inappropriate exercise of authority and biases. This is as we discussed (in Chap. 1) a problem of all times, past and yet to come, because scientifc inquiry is not autonomous, value-free and not neutral and is not guided by the invisible hand of the Legend who tells us how best to allocate our public and private funds. Longino offers at the very end of the book a set of questions that demonstrate that she sees a lot of problems here for philosophers to work on for instance how goal-oriented inquiry and *'different kinds of goal might affect philosophy and knowledge and practices*. She goes one step further and involves in these questions '*the institutional organizations and how they affect the content of knowledge'* and asks '*How can a society use science to address problems when scientifc goals and community structures are not mutually aligned? These questions bring out the political dimensions of science and broaden our conception of what philosophy of science can be about.'*

Finally, she asks *'What kinds of institutional changes are necessary to sustain the credibility, and hence value, of scientifc inquiry while maintaining democratic decision making regarding the cognitive and practical choices the sciences make possible and necessary*? *The fate of knowledge rest in our answers'.*

With these questions, that almost all philosophers of science like Popper consider '*beyond their epistemology* or *theory of knowledge and deliberately bypass',* we return to the main problems addressed here: how does the Legend still determine the ideas and politics of scientifc inquirers which distorts the collective of scientifc inquiry, causes the current problems of science. Legend and its legacy has detrimental effects on our interaction with society and their publics and thus the knowledge we produce, this is 'the fate of knowledge' Longino is concerned with. Longino, after her own struggle with the dualism of the Legend, boldly has been going where sociologists, physicists, chemists, historians, even anthropologists, but few philosophers have gone before. Still, the reviewers of the book who praised her for that, criticize her for not presenting a detailed epistemology. Longino knew how the work of Dewey and James had been received by the 'real analytical philosophers' of their times, that must have offered some consolation.

# **2.3 Conclusion**

# *Towards a Realistic Pragmatist View of Science, Natural Science and Social Science and Humanities*

**From the late 1960s philosophers, sociologist and historians of science gradually, but defnitely showed the Legend of the 'Scientifc Method' to be untenable:**

# **References**

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Bernstein, R. J. (1983). *Beyond objectivism and relativism: Science, hermeneutics, and praxis*. Basil Blackwell.

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Toulmin, S. (1972). *Human Understanding*. Clarendon Press.

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Zuckerman, H. (1989). The other Merton thesis. *Science in Context, 3*, 239–267. https://doi. org/10.1017/S026988970000079X

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# **Chapter 3 Science in Transition How Science Goes Wrong and What to Do About It**

**Abstract** Science in Transition, which started in 2013, is a small-scale Dutch initiative that presented a systems approach, comprised of analyses and suggested actions, based on experience in academia. It was built on writings by early science watchers and most recent theoretical developments in philosophy, history and sociology of science and STS on the practice and politics of science. This chapter will include my personal experiences as one of the four Dutch founders of Science in Transition. I will discuss the message and the various forms of reception over the past 6 years by the different actors in the feld, including administrators in university, academic societies and Ministries of Higher Education, Economic Affairs and Public Health but also from leadership in the private sector. I will report on my personal experience of how these myths and ideologies play out in the daily practice of 40 years of biomedical research in policy and decision making in lab meetings, at departments, at grant review committees of funders and in the Board rooms and the rooms of Deans, Vice Chancellors and Rectors.

It has in the previous chapters become clear that the ideology and ideals that we are brought up with are not valid, are not practiced despite that even in 2020 they are still somehow 'believed' by most scientists and even by many science watchers, journalists and used in political correct rhetoric and policy making by science's leadership. In that way these ideologies and beliefs mostly implicitly but sometimes even explicitly determine debates regarding the internal policy of science and science policy in the public arena. These include all time classic themes like the uniqueness of science compared to any other societal activity; ethical superiority of science and scientists based on Mertonian norms; the vocational disinterested search for truth, autonomy; values and moral (political) neutrality, dominance of internal epistemic values and unpredictability regards impact. These ideas have infuenced debates about the ideal and hegemony of natural science, the hierarchy of basic over applied science; theoretical over technological research and at a higher level in academic institutions and at the funders the widely held supremacy of STEM over SSH. This has directly determined the attitudes of scientists in the interaction with peers within the feld, but also shaped the politics of science within science but also

with policy makers and stakeholders from the public and private sector and with interactions with popular media.

Science it was concluded was suboptimal because of growing problems with the quality and reproducibility of its published products due to failing quality control at several levels. Because of too little interactions with society during the phases of agenda setting and the actual process of knowledge production, its societal impact was limited which also relates to the lack of inclusiveness, multidisciplinarity and diversity in academia. Production of robust and signifcant results aiming at real world problems are mainly secondary to academic output relevant for an internally driven incentive and reward system steering for academic career advancement at the individual level. Similarly, at the higher organizational and national level this reward system is skewed to types of output and impact focused on positions on international ranking lists. This incentive and reward system, with fawed use of metrics, drives a hyper-competitive social system in academia which results in a widely felt lack of alignment and little shared value in the academic community. Empirical data, most of it from within science and academia, showing these problems in different academic disciplines, countries and continents are published on virtually a weekly basis since 2014. These critiques focus on the practices of scholarly publishing including Open Access and open data, the adverse effects of the incentive and reward system, in particular its fawed use of metrics. Images, ideologies and politics of science were exposed that insulate academia and science from society and its stakeholders, which distort the research agenda and subsequentially its societal and economic impact.

# **3.1 The Royal Response (1)**

In the fall of 2012, there were a few high-profle academic public events that were related to the discovery in the year before of a few serious fraud cases in The Netherlands in biomedicine and social psychology. The latter case was shocking and notorious for how it had been done with unfinching arrogance over many years. Because of its size and impact, it became worldwide known. I was present at the meeting held in September at the Royal Academy of Arts and Sciences where Kees Schuyt, a prominent sociologist and law scholar, as chair of a committee of the Royal Academy presented the advice that was focussed on responsible handling of research data (KNAW, 2012). The conclusions of the advice and of the meeting at the Royal Academy was that fraud and violation of the principles of integrity in research was believed to be very rare, but that it should be investigated. The feeling was that education of researchers about integrity, but also in the institutions technical proper handling of data should be promoted and enabled. Very cautiously the idea was mentioned of the obligation for researchers to making data available that supported claims in a journal paper to improve peer review. Finally, it was concluded that informal peer pressure in the community and in the later stages more formally through peer review should be improved. Despite a classical reference to the 'leading values of science which are distinct from any other social activity' and cautious conclusions, the committee did pose a series of critical questions that they believed should not be evaded. They suggested that the social system in which individual researchers do their work might allow or even invite misconduct. In that context they mention the incentive and reward system with its academic hierarchies and publication pressure (p60). The panel with members of Academy and Young Academy largely agreed. Of interest was the mentioning of some examples of serious fraud in physics (amongst others 'the Schön' case). In response to this, a very senior Royal Society member from the natural sciences remarked that of course this issue of quality is typical for *'the soft sciences and biomedicine, but not for us in the hard sciences, because in physics, through our experimentation, we ask a question to nature and nature gives a clear answer, so physics is beyond fraud'*. The chairman, a theology scholar who early in his career had become a professional university administrator, who knew about the problem of foundations, decided to let that one go. At the conclusion of the debate, I made a short critical remark from the foor, that something is really wrong with science if we focus on the rare fraud cases but are looking away from to the growing evidence of a large 'grey zone' of shoddy science, also in other disciplines than biomedicine and social psychology. This grey zone is not populated with fraudsters or bad people who are to blame, but honest researchers that try to survive in our crazy academic system driven by perverse incentives and rewards. This I thought should be acknowledged and discussed. What I had in mind then was in fact to become one of the corner stones of Science in Transition and of this book. The chairman's reply was 'that may be so, but we cannot change a whole system' and then there were drinks, gossip and appetizers (typically Dutch 'bitterballen') in the foyer.

Kees Schuyt was interviewed in a national newspaper and to my relief was much more open about the likely systemic cause of the problems. In October at a meeting held in Spui 25, a University of Amsterdam open podium/debate centre, Huub Dijstelbloem took part in the panel discussion with Kees Schuyt and Andre Knottnerus an authority in the Dutch health science and governmental science advice system. The debate was much more open and critical and did not evade the problems of the system.

November 28, 2012, at the Royal Academy again, a committee chaired by Pim Levelt, a former President of the Academy, presented its investigation of fraud and misconduct of Diederik Stapel. (https://www.rug.nl/about-us/news-and-events/ news/news2012/stapel-eindrapport-ned.pdf). This case, together with a case at Erasmus Medical Centre, since their discovery in September and December 2011, dominated the debate about trust in science in the country. The committee revealed the technical and methodological aspects of the case in great detail. In their fnal comments they state that '*Committees that have evaluated the research of social psychology, have not recognized some of the signals that the committee in this*  *report do describe. They simply were relying on peer review both with respect to methodology and contribution to theory. Another issue in this context is to what degree these evaluation committees are instrumental in sustaining the assumed undue publication pressure and connected mores and behaviours. This specifcally concerns requirements of numbers of publications, the order of authors, responsibilities of co-authors and repeated publication of similar results.' (translation FM).*

#### **The Science in Transition Team**

A year later in November 2013, the public start of *Science in Transition* took place at the same prestigious venue of the Royal Academy of Arts and Sciences on one of the channels in the centre of Amsterdam. The *Science in Transition* team started its work in January 2013. Huub Dijstelbloem, whom I already mentioned, had the years before been very active in national debates about incentive and rewards focussed on inclusive indicators and methods for evaluation of the impact of research. He also studied public participation and policy making which is discussed in Chap. 5. The other three members of the group that started *Science in Transition*, were Jerome Ravetz and professors Frank Huisman and Wijnand Mijnhardt. The fve of us did not really know each other, but we shared our thinking about science which brought us together.

Jerome Ravetz (1929), Jerry, as we call him, replied promptly and enthusiastically, full of energy looking for action when I had send him in the fall of 2012 my little book about science, *Science 3.0, Real Science, Signifcant Knowledge* (Miedema, 2012). I did not know him, but knew his 1971 book (see Chap. 2). Ravetz with a small group of colleagues had published in 1993 a paper in which they described another way of doing science, explicitly with the aim to deal with policy issues of high risk and high uncertainty for science is critical but for which the time for deliberation is limited. They coined the name *Post-Normal Science* for an approach in an integrated and democratized process in which all relevant knowledge and social values and the relevant publics are fully acknowledged and participate (Funtowicz & Ravetz, 1993). In the months that followed Jerry received a Fellowship of the Descartes Centre of Utrecht University which brought him and his wife frequently to Utrecht. His frst visit was to Amsterdam on January 4, 2013 when we talked the whole day and part of the evening about his work, his thoughts about science in 2013 and the actions to be taken.

(continued)

Frank Huisman, Huub Dijstelbloem and Jerome Ravetz. (Amsterdam, February 2013)

Frank Huisman (1956) is at Maastricht University, the interdisciplinary group of Science, Technology and Society Studies (MUSTS) and since 2006 full professor of the History of Medicine at UMC Utrecht. His interest is the history (and sociology) of modern medicine. Together we started in 2009 a selective advanced PhD course on philosophy and sociology of science, called *This thing called Science.* The course proved to be an immediate success: 120 PhDs applied to be enrolled in the course which offered place to only 45 of them, and students declared it to be the best course offered by the Graduate School of Life Sciences. There was clearly a great need among some PhD students to learn about the history, philosophy, ethics and politics of science, and be socialized into the biomedical sciences in a different way. We felt very happy to be able to create this new awareness among a new generation of biomedical researchers.

Frank Huisman introduced Wijnand Mijnhardt (1950) to me at the end of November.

Wijnand Mijnhardt is an international well-known historian of culture and science and at that time served as Chair of Comparative History of the Sciences and the Humanities. He is founder and past director of the Descartes Centre for the History and Philosophy of the Sciences at Utrecht University. I told Wijnand I was honoured that he came to my room and I pulled his leg stating that '*his Centre, to the best of my knowledge, preferably studied scientists and scholars that had already passed away a long time ago. I understood, I said, that this nicely avoids the political issues that in our time trouble academia and society, but*', I said, '*my goals are quite the opposite. Our thinking about science should, in the good tradition of pragmatism lead to action in the real world to improve the academic lives of our stakeholders: graduates, post-docs, students and professors in our universities and those in society alike'.* Wijnand appreciated the humour and loved this idea for the project. He in the following years eloquently brought to the table his strong opinions with colourful favours in the context of *Science in Transition*.

Sarah de Rijcke, photo taken by Bart van Overbeeke

Regarding the composition of the team, we were criticized and had to admit, that we had a problem: we were fve, and later four, older white males who each had done well in the system. This was corrected in part very soon, when Sarah de Rijcke a well-known researcher in STS at CWTS Leiden and an expert on all the issues Science in Transition was addressing joined the team. We did not have graduate students or early career scientist in the team. Our best defence to this was that, given the idea that changing a social system goes against the elites and the most powerful in that very system, we were not vulnerable to the classical framing of 'being a couple of losers complaining about the system in which they had failed'. Many who question the mores and rules of the system indeed are told 'If you cannot stand the heat, get out of the kitchen'.

# *Science in Transition*

We started from the optimistic, some thought naïve, perspective of the possibility to improve science. Our analysis of the problem had a broad scope, from quality issues, fraud, poorly conducted or irrelevant science, agenda setting and responsiveness to issues in society, assumptions, ideologies and hierarchies that distorted the system internally in academia and in interaction with society. We wanted at all cost to avoid the well-known type of general academic discussions about problems of 'the university' and easy blaming of 'incompetent' administrators, lazy students or neoliberal economics'. Angry complaining and blaming without realistic directions for improvement would stife our initiative like has happened to many initiatives before. For all of us it was clear that these problems had to be approached in a larger context of the socioeconomics of the institutional organization of science. From the start it was clear that we needed to more specifcally discuss the contribution of the incentive and reward system. Persistence of specifc problems, in our view, seemed to be related to the system of research evaluation in institutions and by funders as it had gradually developed since the 1980s. Our focus was very much on research, but in the incentive and rewards structures in academia this related to the poor appreciation of teaching and teaching careers and so this was discussed as well.

All of these issues one by one were not new, but we believed that an integral approach of the issues seen as parts of one social system was going to be quite unique. Many science writers and philosophers discussed their favourite views and worries, but a consistent system approach to science to our knowledge was very rare, if available at all. Apparently, without such an explicit awareness, we felt confdent as a team to have enough complementary experience in science and academia, both in theory and practice, to take on this ambitious project. We decided that we had to get a proper analysis and comprehensive picture frst. We agreed that going from there, to achieve long-lasting improvements, concerted actions of the community were required. This involved systemic institutional change in which academic leadership at universities, especially from Rectors, Deans, Royal Academies and prominent scholars, public and private funders should be engaged and committed.

Three workshops were held on *Image and Trust, Quality and Corruption, Communication and Democracy* in April, May and June 2013. Next to the initiators, about ten scientists from the Netherlands were invited to participate in each of the workshops. Participants were hand-picked by us, known for their expertise, critical thinking and outspoken views about science. (See website scienceintransition.nl for the lists of participants and the workshop presentations.) Based on the results of these three workshops in the summer of 2013, a draft position paper was produced by the initiators, mainly by exchanges via the mail.

# **3.2 The Royal Response (2)**

We were not alone in this endeavour. In the Royal Society, in that same period, a committee was working on a report on trust in science. With reference to the recent high-profle fraud cases, the Ministry of Education, Culture and Science (OCW), in January 2012 had formally asked the Royal Academy to advise the Ministry regarding trust in science. In it there was a specifc request to advice on possible actions by the main actors in the domain of science, including research institutes, funders and government, that could help improve integrity and trust. This committee started in March 2012 and published their advice in May 2013. The report was presented in May 2013 by the committee chaired by Keimpe Algra, a humanities scholar, who was to become Dean of the Faculty of the Humanities of Utrecht University the next year (KNAW, 2013). The committee in response to the questions from the Ministry had taken a broad approach, explicitly including the wider system and community of science. They concluded that the Mertonian rules were under pressure because of changes in the scientifc system that had occurred in the past 30 years, with consequences for the practice of research. This agrees with the analysis of the legacy of Merton presented in Chap. 2. From this analysis the committee concluded that there is, with respect to integrity and quality, a duty for the individual to show '*honesty about the research goals and intentions*'. At the same time and with even more emphasis the institutions, universities and funders were urged to take responsibility for the culture of science where it did not promote or even obstruct proper behaviour and integrity of researchers. A couple of times the committee suggested that it would be a good idea to have institutional accreditations for research to help the institutions in setting up and uphold the relevant practical policies. The example of quality assurance policies in health care were mentioned. Although the committee was cautious with respect to top-down programming of research, they made it clear that not only should research be done right, but also the right research should be done, which brought 'agenda setting' and external values as a novel dimension in the discussion. It was proposed to invest in more practical awareness and social control in the form of positive peer pressure with important roles for the research communities in universities and research institutes. For this, they said an open and safe academic culture was required.

The committee, in contrast to previous reports discussed the problematic effects of the external forces on the practice of academia. This related to allocation of funds and collaborations with private commercial partners. The increasing infuence on academic life also of tenured staff, of short-term funding schemes, being focussed on 'sexy topics and hypes' and the researcher's temptation to promise unrealistic impact and novelty were mentioned as a distortion of the dynamics of academia. This induced bias against replication and negative results, also at the journals, goes against long term more diffcult research. The committee states that this is refected in national research evaluations which enforces these practices and on a focus on numbers of publications. Concluding with constructive suggestions, the committee did not suggest to really rethink the issue of cause-and-effect regarding the problems discussed. They were nearly there but did not take that logical next step to conclude or at least suggest that the institutional organization with its incentive and reward system, and specifcally its indicators for excellence, critical for decisions on funding and career advancement might provoke strategic behaviours that caused or at least promoted many of these interdependent problems.

This advice, *'Trust in Science',* was discussed at a meeting at the Royal Academy in September 2013 where I was invited to give a talk and presented the Science in Transition Position Paper and *'A Toolbox for Science in Transition'* to reassure the audience, of mainly early career scientists, that national and international change was possible (Supplement 1).

# **3.3 Science in Transition Position Paper, October 2013**

A fnal version of the Position Paper, incorporating comments that we had received thus far was published on the website on October 17, 2013.

https://scienceintransition.nl/en/about-science-in-transition/position-paper

The Position Paper is composed of the chapters: Images of Science, Trust, Quality, Reliability and Corruption, Communication, Democracy and Policy, University and Education, and a brief Conclusion paragraph.

# **3.4 Science in Transition: A Systems Approach**

*Science in Transition* as an initiative and movement to improve the impact of science and research entered a feld where many had gone before. We were heavily inspired and infuenced by many different scientists and scholars who had been writing about science and society, as the reference list of the Position Paper duly refects. These writings and actions go back to the 1970s and deal with the ideology of science and its Legend, the sociology and social organization of science and with problems of science in and with society. In the years before 2012, major initiatives with respect to quality and reproducibility in research had started. This in reaction to the increasing evidence from empirical research showing poor quality and unexpectedly low reproducibility in biomedicine and psychology, but also other felds of research (Altman, 1994; Begley & Ellis, 2012; Prinz et al., 2011) (Ioannidis, 2005; Ioannidis et al., 2012; Mofftt et al., 2011; Moore et al., 2017; Nosek et al., 2012). I will not discuss the history of this meta-science work on poor quality research and replication, as that has been done by experts before. Our interest in the context of *Science in Transition* was to understand why poor research is being done and published. It had not

been decreasing even as we know about it but had apparently rapidly been increasing to be a problem in the more recent years. Many studies had already shown the relation between the use of bibliometric indicators in research evaluation, thus in the incentives and rewards system and strategic behaviour of researchers (Hammarfelt & de Rijcke, 2014; Moore et al., 2017; Wilsdon, 2016; Wouters, 1999, 2014; Wouters et al., 2015).

It is this problem that is, more implicitly though, addressed by the San Francisco **D**eclaration **O**n **R**esearch **A**ssessment, known by its acronym **DORA**, that started in December 2012:

*There is a pressing need to improve the ways in which the output of scientifc research is evaluated by funding agencies, academic institutions, and other parties. To address this issue, a group of editors and publishers of scholarly journals met during the Annual Meeting of The American Society for Cell Biology (ASCB) in San Francisco, CA, on December 16, 2012. The group developed a set of recommendations, referred to as the San Francisco Declaration on Research Assessment.*

The debate about quality and impact of research in biomedicine reached a novel international level in January 2014 with a series of articles under the heading *Research: Increasing Value, Reducing Waste* in the *Lancet* on January 8, 2014. This was the result of an initiative of a group of very established biomedical researchers, who in some case already for many years had focussed on quality issues related to methodology, design and problem choice in clinical studies in humans, but also in animal studies. Internationally the best known are: John Ioannidis (METRICS Stanford University), Doug Altman (Oxford University), Ian Chalmers (Oxford University) and Paul Glaziou (Bond University) (http://www.thelancet.com/series/ research) and the initiative is called *Reward Alliance* (http://rewardalliance.net/ increasing-value-reducing-waste/).

In the same month, a paper was published in *Nature* by the NIH leadership, Francis Collins and Lawrence Tabak, announcing the NIH reproducibility project. This project is an adequate reaction to the seminal study by Begley and Ellis published 2 years before also in *Nature* on poor reproducibility of pre-clinical biomedical research published in *Nature, Science* and *Cell* and an earlier study by Prinz et al. This was boosted in March 2012 by a paper in PNAS with the ominous tittle Rescuing *US biomedical research from its systemic faws, w*ritten by fve very high-profle authors, from the US biomedical science community. The bestknown authors included Bruce Alberts, a former long-serving editor of *Science,* Shirley Tilghman a former president of Princeton and Harold Varmus, a former Director of NIH, former president of Memorial Sloan Kettering Cancer Centre and then director of the National Cancer Centre of NIH and last but not least the 1989 Nobel prize winner (https://www.pnas.org/content/111/16/5773).

# **3.5 How Scientists Get Credit**