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When I entered Cornell’s Ph.D. program in Science and Technology Studies in 1997, Structure of Scientific Revolutions was naturally one of the first books I was assigned. I came into the program with a bachelor of arts in engineering, so perhaps I was predisposed to appreciate Kuhn’s lively mélange of the humanistic and the technical. Kuhn did me a bit of a disservice, though, in that his writing was so clear, readable, and relevant to both what I knew and what I wanted to know more about that he set the bar very high for anything else I would read (or write!). Certainly, few books since then have matched Kuhn in setting forth a bold, intelligible argument in such an engrossing way. Still, I look back on that first reading of Kuhn as a sign that I made the right choice to be in a field where I work alongside other scholars who also look back at Kuhn as a common point of reference.

Curiously, it was the early chapters of Structure on normal science that really spoke to me and that continue to inform my work. I think it’s clear that Kuhn’s own ambitions had more to do with the later sections on revolutionary science , and certainly those are the ones that have generated the most heat. But, back in the late 1990s, to this lapsed engineer and aspiring laboratory ethnographer, the differing logics of normal science across time, culture, and discipline seemed a much more fruitful line of investigation than the endless and acrimonious debates about incommensurability, relativism, and the uncertain reality of reality (e.g., Koertge 1998; Labinger and Collins 2001).

Not, of course, that the line of work that spun off from Kuhn’s thoughts on revolutionary science hasn’t been extraordinarily generative. Particularly influential for me in that regard has been the long, rich tradition of so-called “controversy studies” associated with the “strong” Edinburgh school version of the Sociology of Scientific Knowledge (e.g., Mackenzie 1990; Shapin 1975; Edge and Mulkay 1976) as well as the so-called Bath and York schools (Collins and Pinch 1982; Pinch 1986; Ashmore et al. 1989). Even in these studies of potential paradigm shifts, however, the persuasive force and many of the lessons of the SSK controversy studies depends to a great extent on a close examination of Kuhnian normal science. That’s in part because virtually none of the contemporary controversy studies were able to follow a case of a successful overthrow of some set of major, established scientific facts. Kuhn’s point that revolutions happen so rarely that few scientists live through a paradigm change was seemingly confirmed. Indeed, in order to catch a revolution in progress, sociologists had to resort to historical controversy studies, such as Steven Shapin and Simon Schaffer’s Leviathan and the Air-Pump (1985).

More subtly, my early reading of the SSK controversy studies suggested, to me at least, that the whole argument of this genre depended on the discovery that the seeds of uncertainty, controversy, ineffability—seeds that sprout during times of revolution—are present but relatively unproblematic during times of normalcy.Footnote 1 Take, for instance, Harry Collins’ (1985) Changing Order , a three-part study of applied scientists building a laser, astrophysicists building and debating gravitational radiation flux detectors, and parapsychologists trying to communicate with plants. Like Kuhn, Collins is quite obviously more interested in revolutionary than normal science—hence the changing order of the title, as well as the subsequent four decades and several thousand published pages of text in which Collins has stuck with his gravitational radiation researchers in hopes that they will unearth something paradigm-changing.

Collins’ argument about gravitational radiation research is that it is such a complex endeavor that its practitioners are unable to describe all of its intricacies even to each other. Even if they could, he claims, there is a great deal of tacit knowledge embedded in gravitational radiation flux detectors that is beyond the conscious grasp of even those who possess it, and which is therefore only contingently available to inflect debates about whether a particular detector is working properly and has or has not detected the passage of a large gravitational wave. That argument has been contentious, and even Collins has retreated from his less cautious formulations of it (Collins and Evans 2002).

Yet the normal-science preamble to that part of Changing Order’s argument seems relatively unexceptionable—Collins follows a group of applied physicists as they try to build a TEA-laser in the early days of that technology. They fail repeatedly, even though one of them has built such a laser before and has all the formal knowledge needed to do so again. Eventually, something gets resolved and the laser begins to vaporize concrete—the rather unambiguous measure of whether it is working or not. Yet even though they eventually succeed in a task that, while difficult, is nowhere near the complexity of a gravitational radiation flux detector, the reason why they succeed remains a bit of a mystery. Collins hints, at any rate, that the scientists’ explanation for why the laser suddenly started working is provisional and unimportant to them.

Indeed, it is not uncommon for scientists to volunteer skepticism of their own such explanations in interviews. Here’s an example from an interview I conducted with an early scanning tunneling microscopist describing how he overcame a similar experimental obstacle:

We thought we eventually traced the problem to brass screws which were used in the sample holder. The brass screws contained zinc I believe and apparently the story was—I guess I still am not sure even now that this was what the problem had been—but the hypothesis was that this zinc … in the screws was in a part of the sample holder which got very hot during the part of the cleaning procedure where you anneal the silicon…. Zinc is volatile enough at those kinds of temperatures that you can get reasonable partial pressures in the chamber, maybe not a lot but enough that you could get a fraction of a monolayer of zinc on the silicon. Some of these heavy metals on silicon form silicides and are known to roughen the surface significantly. And we were seeing rough surfaces in which we couldn’t see any particular atomic order…. So once we realized that was a possibility we replaced the screws, sent the chamber back and had it cleaned…. Here’s why I don’t know whether that’s the real explanation, we also changed some other things in that procedure at about the same time and it started to work. So whether that did it or some of the other things we changed did it I’m not sure, and we didn’t really care. That’s not what we were researching. We just wanted it to work.

In other words, Kuhnian normal science is often less concerned with Truth and Knowledge than with getting things “to work.” Scientists might be somewhat more focused on capital-T Truth and capital-K Knowing when embroiled in a controversy or a paradigm shift, but those are exactly the conditions in which everything is messier: the standards for what counts as “working” aren’t settled, both the necessary tacit and formal knowledge are in shorter supply, and the variations among different groups’ experiments are suddenly more salient than usual.

My point here isn’t that Collins’ observations about building a TEA laser confirm what he has to say about gravitational radiation research (or controversial, paradigm-threatening science more generally). Rather, I’m arguing that scientists’ provisional insouciance regarding formal knowledge, and their willingness to endure large gaps in their understanding of how their experiments work, was an important but rather easily replicated and not terribly controversial discovery of SSK. Extrapolating from that discovery to bolder claims about leading-edge science might or might not be warranted, but, at the very least, SSK’s textured view of wild-type normal science made problematic the more totalizing and rigid versions of some of mid-century philosophy’s favorite hobbyhorses: demarcation , unity of science, scientific method, reductionism , the distinction between contexts of discovery and justification, etc. Those early SSK controversy studies didn’t get everything right, obviously; but any contestation of SSK that ignores those studies’ robust empirical findings about normal science—findings that, indeed, scientists themselves routinely echo—is not operating in good faith.

The other major Kuhn-descended genre of science studies that I was introduced to early in graduate school—in fact, the genre I entered graduate school to become a practitioner of—was the laboratory ethnography , as typified by a crop of studies of California labs in the late 1970s and early 1980s: Latour and Woolgar (1986); Knorr-Cetina (1981); Traweek (1988); Lynch (1985). Here, the connection to Kuhn’s description of normal science is even more apparent. “Lab studies” are really just ethnographies of work. Their basic finding is that scientists’ work habits look a lot like those of most other professionals, especially those in occupations that generate, manipulate, or disseminate information and/or that involve tinkering with materials and machines. Scientists spend much of their time writing (Latour and Woolgar 1986), gossiping (Garfinkel et al. 1981), promulgating-resisting-accommodating to bureaucratic rules (Gusterson 1996), venturing out to work sites (Latour 1999), etc. If one adopts the Martian perspective of an ethnographer, it isn’t obvious just from their work practices which inhabitants of a lab are the “scientists” and which are the janitorial or cooking staff (Kelty 1997).

Does the quotidian nature of scientific work matter? Scientists, after all, also do science, which makes them special in the eyes of most late modern people—even if no one can cleanly demarcate science from other kinds of practice. At the least, though, lab studies’ depiction of wild-type Kuhnian normal science gives ammunition to deflationary conceptions of science as, in Andrew Pickering’s words, “practice and culture” (for such a framework, see Pickering 1995; for more examples, see the essays in Pickering 1992). Scientists make judgments in much the same way the rest of us do. Their judgment is considerably better than most regarding their particular patch of knowledge and practice, but that just means that we should extend to scientists the same degree of trust that we extend to experts in law, finance, education, insurance, management, etc. who also employ sophisticated bodies of “practice and culture.”

Again, as with SSK, I am not arguing that laboratory ethnographers were correct in every extrapolation they made from their observations of wild-type Kuhnian normal science to bold claims about controversial or revolutionary science (or the validity of scientific knowledge in general). For instance, I’m sympathetic to (though not entirely persuaded by) Park Doing’s (2009) insistence that laboratory ethnographers have not captured in real time a single instance of the “social construction” of knowledge. That may or may not be the case, and is certainly worth debating.

What’s much harder to contest, though, are the baseline observations of ordinary scientific conduct that ethnographers have established. And from those fine-grained, easily-replicated observations, we now have a pretty good sense that, yes, scientists rely on all kinds of social cues to help them decide whom to trust, what data are robust, which results are important, which arguments are persuasive, etc. “Social cues” here means something like the list of rationale for belief or disbelief that Harry Collins (1985, p. 87) put together from interviews with gravitational radiation researchers:

  • Faith in experimental capabilities and honesty, based on a previous working partnership.

  • Personality and intelligence of experimenters.

  • Reputation of running a huge lab.

  • Whether the scientist worked in industry or academia.

  • Previous history of failures.

  • ‘Inside information’.

  • Style and presentation of results.

  • Psychological approach to experiment.

  • Size and prestige of university of origin.

  • Integration into various scientific networks.

  • Nationality.

Scientists don’t, of course, only rely on such social cues, and their reliance on these cues is usually provisional. As I’ve argued elsewhere (Mody 2010) , “contingent social cues are implicated in the current status of fact claims, in that they are part of a documentary method of interpretation. Scientists integrate what they know about their [and each other’s] organizations and research communities into their understandings of technical measures.”

And vice versa—they integrate their emergent understanding of instruments, theories, materials, experiments, etc. into their evaluations of each other. Again, from Mody (2010): “As the logjam of measures grows, scientists’ understandings of their social worlds (who’s competent, who’s crazy, which disciplines are ‘sloppy’ or ‘careful’) shift, inextricably, with their understandings of nature (such that ‘social’ and ‘natural’ [or ‘technical’] are entangled).” That shouldn’t be a surprising observation, at least not to anyone who has read Kuhn and/or talked with practicing scientists.

Still, it’s not an observation that’s woven into many recipes for “the” scientific method or into prescriptions for the governance of science. Rather, most normative methodological and policy frameworks either ignore scientists’ use of social cues or treat such practices as a particularly unfortunate consequence of the generally unfortunate fact that science is done by human beings. Indeed, the desire to ease humans out of science was an important factor behind the decades-long, and so far failed, attempt to turn artificial intelligence research into a branch of the philosophy of science (Roland and Shiman 2002; Dreyfus 1972, 1992; Collins 1990). Perhaps, ultimately, we will have machine intelligences that can do science—though, at the moment, it looks more likely that such machines will be extraordinarily sophisticated pattern recognizers (á la Siri or the movie recommenders used by Netflix and Amazon) rather than silicon philosophers. Still, that day looks much further away now than it did in, say, 1956.

In the meantime, my contention is that philosophers, historians, sociologists, and anthropologists of science could make a great deal of progress in understanding—and perhaps aiding—science by first acknowledging that scientists rely on social cues for plenty of good reasons. The humanity and sociality of science aren’t perfect, of course, but they also aren’t incidental or unfortunate features of the scientific enterprise. Rather, the lesson from Kuhn—perhaps his most important and robust lesson—is that the humanity and sociality of wild-type science are constitutive of the scientific enterprise as we know it. Human needs and desires, as promulgated through a variety of social formations, furnish the aims of science, the standards by which to recognize who counts as a scientist (and how good they are), the incentives for doing science, the paths to becoming a scientist, the means to do science, etc. Core features of scientific knowledge-making—such as, what counts as “objectivity” (Daston and Galison 2007)— are not set in stone, but have histories that vary over time and place, and are shaped by the aims of the societies that scientists are a part of.

It’s easy to lose sight of that lesson, so long as Kuhn’s contribution is taken to be about “the structure of scientific revolutions.” Since that theme was the title of the book and the focus of Kuhn’s passion, most people accepted that scientific revolutions were the ground on which debate would proceed. Accordingly, most of the conventional arguments over Kuhn’s thesis (and those of his intellectual fellow travelers in science studies) have centered on questions of scientific change: Does science progress?; Do successive paradigms account for more of the world more accurately than their predecessors?; Can the basis for moving from one paradigm to another be (or be made to be) rational?; etc.

The question Kuhn started out with, however, turns those points of debate on their head. He wanted to know why the Ptolemaic system stuck around for as long as it did, despite flaws that were well known to its practitioners, and even well after viable alternatives had been put forward which addressed those flaws. Seen from that perspective, revolutions are merely Kuhn’s stalking horse for exposing the structure of scientific normalcy. That is, if, historically, one can find a set of explanations (a paradigm, if you will) that we today believe was “better” than its predecessor and yet no revolution ensued to put the new paradigm into place, then that is a probe for understanding what the old paradigm achieved that the new one did not. It’s also a probe for reflecting with more subtlety on what we mean when say that one paradigm is “better” than another.

Let me reiterate that point somewhat differently. My reading of Kuhn—as refracted through my training in the “Ithaca school” version of science studies—is that bodies of technical knowledge and practice (again, let’s call them “paradigms”) can achieve a certain obduracy despite the vast number of cogent objections that can be raised against them in part because scientists and engineers are able to make those paradigms workable, on a day to day basis, with respect to some ever-shifting set of aims promulgated relative to their professional communities and/or to various constituencies in the societies of which they are a part. That is, normal science keeps going, despite obvious anomalies and ignoration of open questions, because normal science achieves many more goals than just the clearing away of anomalies and open questions.

Thus, Kuhn offers a persuasive justification for putting to one side—or, at least, putting on the back burner—the question of how scientists and engineers ought to work, and instead gives us the grounds for asking how they actually do work. Normal science, despite all its flaws, is sustainable most of the time because it achieves something—not necessarily a more perfect picture of reality or an incontestable ontology or an ironclad method for generating new knowledge, but still, something that scientists and their patrons care about. So Kuhn allows us to ask—what is that something, and what does it tell us about science and its stakeholders?

In my own research and teaching, I often use a question and a very rough rule of thumb to try to identify what that something (or, usually, those somethings) might be for any given case. The question is the one in my title: what do scientists and engineers do all day? It’s not, I think, a question that Kuhn himself would’ve asked, but it is a question that follows quite easily from his foregrounding of such mundane bits of scientific life as textbooks and problem sets. That is, Kuhn wasn’t just interested in scientists’ published works and polished statements, in which the messy tangle of quotidian demands has been scrubbed clean. Rather, Kuhn wanted to show that a paradigm informs and is emergent from every aspect of a scientist’s life, even those aspects that the analyst might assume aren’t germane to scientific knowledge .Footnote 2 Thus, Kuhn built his whole argument around the ordinary stuff of scientific practice—the stuff too common or too ephemeral to have garnered much attention before.

Those who followed him took that preoccupation with the ordinary, unfinished flotsam of scientific life even further. “What do scientists do all day?” is a question that can be read quite easily into most of the groundbreaking works of science studies of the past forty years. As I’ve indicated, it shines through in the laboratory ethnographies and controversy studies discussed above. It informs to a great extent the wonderful ethnographically-textured laboratory histories of the 1990s such as Image and Logic (Galison 1997) or Lords of the Fly (Kohler 1994). It’s a question that hovers around the post-Kuhnian close inspection of tacit knowledge (Collins 2010), visual representation in science (Lynch and Woolgar 1990), laboratory notebooks (Holmes 1990), patents (Bowker 1992; Swanson 2007), and so on.

In my own work—particularly in conducting oral history interviews but also in reading through archival materials—I’ve tried keep that question front and center. And I pair with it a rule of thumb that’s certainly fallible but perhaps still useful. Namely, if scientists and engineers spend a significant part of their day, or a significant part of their cognitive or emotional capacity, on X, then maybe X is important in the practice of science and engineering in their mutual shaping of (and by their society in the construction of) technical knowledge , and in the achievement of a variety of aims relative to scientists’ and engineers’ professional communities, home institutions, networks of personal affiliates, and segments of the societies they live in—even if, at the outset, X seems to have little to do with “Science” with a capital S.

So, for instance, if academic (and corporate and government) scientists and engineers spend a lot of time on teaching, well, maybe that’s important. As David Kaiser and I (Mody and Kaiser 2008) have pointed out, most work in science studies ignores the pedagogical context in which much science takes place. That’s perhaps in keeping with the ideology of science, as voiced, for instance, in Nobel lectures (Traweek 1988), where scientists often downplay their roles as teachers, students, and mentors. With explicit reference to Kuhn, though, Kaiser (2005a, b) has argued in his own work (and by editing and otherwise calling attention to the work of others) that teaching is important to science in many ways, not least in the creation of new knowledge. The classroom and the textbook and the mentoring relationship are sites where scientists advance arguments, where they discover and develop new ideas, and where they have a prime opportunity to engage their society’s rather reasonable worries for the next generation’s prospects.

Similarly, what if some scientists and engineers spend a lot of time writing popular books or consulting on blockbuster films? Well, maybe we should take that seriously as part of their efforts to achieve the aims of their normal science. Indeed, people like Gregg Mitman (1999) and David Kirby (2011) have done great work showing how, again, engagement with larger, popular audiences is not a distraction from scientific work. Rather, it is scientific work that offers researchers access to resources, a chance to try out ideas, to recruit new personnel, and to get a leg up in controversies with their colleagues—as well as a means to achieve important further aims, such as becoming famous.

What if we find that scientists and engineers spend a lot of time at conferences (Mody 2012; Ochs and Jacoby 1997) ? I find this to be a weirdly neglected topic in science studies, since if the “social construction of knowledge” is observable, then it would have to be observable at scientific conferences—these, after all, are the occasions when scientists are both at their most social and most directly concerned with hashing out whose knowledge is correct. What if we find that scientists and engineers spend a lot of time traveling? That’s a theme historians and anthropologists have picked up on for the field sciences (Kohler 2002; Helmreich 2009), but theoreticians and lab scientists travel as much as anyone. Why, and what do they accomplish by travel? What if we find that scientists and engineers spend a lot of time writing proposals or polishing appeals to their bosses or funders (Myers 1985)? Is that just a necessary evil, or is that what normal science is in a complex, heavily technological society where scientists and engineers make their normal science sustainable by attaching it to the concrete aims of politicians, bureaucrats, philanthropists, etc.? What if we find prominent scientists and engineers spending almost none of their time “in the lab,” but instead managing their subordinates, traveling, writing grants, doing administrative work for the employers, etc. (Knorr-Cetina 1999)? Are they no longer “real” scientists or engineers? Or are they simply practicing their normal science by gathering resources and personnel and political goodwill?

More central to the present concerns of historians and sociologists of science is the discovery that many scientists spend much of their days participating in politics in one way or another—taking roles in government (Wang 2008), becoming activists (Moore 2008), pronouncing on the grand debates of their day (Egan 2007). Again, are such activities a distraction from “real” science? Or does Kuhn give us the tools to say that normal science is sustainable despite anomalies in its worldview partly because it achieves the aim of underwriting (or, occasionally, undermining) statecraft and political order? There are now several different keywords for describing that mutuality of science and politics. There’s the “co-production” of knowledge and political order associated with Sheila Jasanoff (2004), sometimes with a nod to Leviathan and the Air-Pump . There’s the Latourian actor-network (Latour 1987), in which the set of scientifically-known and technologically-made actors and actants is at the same time a kind of Parliament. There’s the Foucauldian strand of science studies, probably best exemplified by Paul Rabinow (Rabinow and Dan-Cohen 2005), in which conceptions of self, morality, common sense are constantly remade by what we know and what we can build. And more! Science studies is now a field where the entanglement of social and scientific change is a given, in a way that Kuhn doesn’t really gesture to in Structure, but which we would’ve been much slower to appreciate without him.

All that attention paid to the politics of/in science has to some extent distracted from other aspects of normal science, but there’s still plenty to say. We now have some extraordinarily fine-grained studies of just how much normal science is shaped by completely ordinary activities that are largely conducted without any thought as to their scientific import. For instance, over the past twenty years or so, historians of science and technology have arrived at some rather counterintuitive conclusions from the mere fact that scientists and engineers eat and drink. I remember being warned in graduate school that the “what do scientists do all day” rule shouldn’t be taken too far, since it couldn’t possibly matter what a scientist ate for breakfast. Yet, as Steve Shapin and others (Lawrence and Shapin 1998) have shown, the scientist’s credibility, and his or her ability to carve out a role of authority in their society, may indeed depend on what they eat or don’t eat. One of the great discoveries of science studies is the degree to which scientific discovery and technological innovation may be the upshot of a conviviality that the participants may engage in for all kinds of other reasons – whether they be botanists in English pubs (Secord 1994), copier repair technicians in diners (Orr 1996), or electrical engineers creating Silicon Valley over ham radio sets or drinks at the Wagon Wheel bar (Lécuyer 2006). I would note with some pride that the index of my own history of scanning probe microsocpy (Mody 2011) lists two occurrences under the entry for “beer.”

In a slightly different vein, Michael Lynch, Simon Cole, Ruth McNally, and Kathleen Jordan (Lynch et al. 2008) have coined the term “sub-normal” science to describe occupations that are manifestly technical—that require some sophisticated scientific expertise—and yet which are so routine as to be completely insulated from the possibility of revolution and paradigm shift. The particular case they have in mind is forensic science, especially DNA “fingerprinting,” but the space of sub-normal science is quite large—possibly several times as large as the space of “normal” science. Think of all the national metrology institutes that set standards for every mundane food and substance (Lezaun 2012), or ministries of agriculture randomly testing crops and meat for disease or regulated substances (Lezaun 2006), or quality control laboratories in dairies and breweries. Sub-normal science deserves considerably more attention than it has received thus far, in part because, as Philip Mirowski (2011) has argued, it may be crowding out “normal” science. Sub-normal science is cheaper and more predictable than normal science, and therefore in some ways preferable to commercial concerns. Thus, firms in some industries—particularly in pharmaceuticals and other biomedical sectors—have outsourced more and more of their research to contract research organizations. If Mirowski is right, this shift poses a grave threat to normal science’s capacity to unpredictably surprise and discover.

At the other end of the spectrum, we’ve also learned a great deal recently about all the different ways that seemingly abnormal science is in fact critical to the normal scientific enterprise. Historians and sociologists have found scientists and engineers spending much of their time and energy obsessed with seemingly quite unscientific—even purportedly antiscientific—ideas, and yet also enormously productive in the eyes of many of their contemporaries. For instance, Andrew Pickering (2010), Matt Wisnioski (2003), Thierry Bardini (2000), and others have shown how top-shelf researchers (psychologists, engineering scientists, mathematicians, etc.) immersed themselves in the countercultural world of drugs, mysticism, and avant-garde art in the late 1960s and 1970s. More recently, there have been a few notable cases in the field of nanotechnology of very prominent biologists and chemists espousing young-earth creationism, or something very close to it. Kaiser (2011), again, has recently shown that one of the most active and respected areas of physics research today—quantum entanglement and Bell’s Theorem—was only rescued from the dustbin of disciplinary neglect by a rag-tag group of “hippie” physicists in the early 1970s because of their (to them) related interest in ESP, astral projection, time travel, UFOs, and communication with the dead.

Note that all this was happening in living memory, rather than in the time of Newton and Boyle! Ought we to ‘tsk tsk’, as previous generations did about Newton’s alchemy and theology? Or should we take these activities and beliefs seriously as something some scientists and engineers care deeply about, that they see as integral to their conception of what science is and what purpose it serves, and that they mine for ideas, skills, resources, and connections?

Normal science, sub-normal science , abnormal-but-still-productive science—these and the other areas I’ve surveyed are all topics that have followed naturally from the research program set in motion by Kuhn—or, perhaps by those researchers who re-discovered Ludwik Fleck ([1935] 1979) as a result of Kuhn. However, there have been a few areas where Kuhn’s preoccupations have hindered our appreciation of some pervasive and, frankly, quite important aspects of normal science. Let me raise two of these, one more in science studies and the other more in technology studies.

First, in science: if we apply the “what do scientists do all day” rule, we’ll find, among other things, that a great many scientists and engineers spend a lot of their time taking out patents, starting companies, working for or consulting with firms, agitating for universities or government labs to found tech transfer offices, etc. There are many post-Kuhnians who would like to ignore those activities, as Kuhn did. There are a few loud voices in our field who decry such activities and who even find the study of such phenomena suspicious.

It seems to me, though, that the properly Kuhnian task, for our present age, is to ask what scientists and engineers (and the organizations that employ them) get out of such activities (especially since profit is often not one of the outcomes). As Steve Shapin (2008), Paul Rabinow (1996), and many others—including, I hope, myself in some way—have concluded, entrepreneurial science isn’t necessarily problematic science. Indeed, engagement with the marketplace can enable certain grounds for creativity and persuasion that make for very good science. Industrial and entrepreneurial science weren’t interesting to Kuhn, and that lack of interest is one of his less positive legacies that our field is still working through. But the study of industrial and entrepreneurial research, at least as I would encourage my colleagues to approach it, is very much in the vein of figuring out what most Kuhnian normal science is like.

Similarly, in technology studies, we’re hampered by an obsession with technological revolution that isn’t, of course, solely traceable to Kuhn but which Kuhn’s work has fostered. One piece of evidence for this, I think, is the widespread use of “paradigm shift” as a buzzword in the business world. I’d point in particular to David Edgerton (2007) as someone who’s provocatively and usually correctly criticized science and technology studies for its infatuation with revolution. As Edgerton has argued, in science studies we talk too much about research at the expense of development, and in technology studies we talk too much about innovation at the expense of use and maintenance (and even when we do talk about use, we’re usually focused on new or innovative users, rather than “normal” use).

Now, I’m not going to pretend that asking “what do scientists and engineers do all day” always yields interesting answers. There’s as much time wastage in science as anything, so much of what scientists and engineers do all day has little bearing on anything. Though I suspect that time wastage in science might indeed play an important role in knowledge creation—there’s a great study waiting to be done of boredom and idle time in science. I won’t pretend, though, that we should only be asking what scientists and engineers do all day, since much of what any of us does is framed by a social order that rarely explicitly impinges on our actions and which we may not even be aware of. Nor do I pretend that the kinds of answers to that question that I’ve just outlined are very original—these are the kinds of things historians, sociologists, and anthropologists of science have been working through ever since Kuhn.

But if we keep that question at the ready, and if we push ourselves to revisit it in fresh ways, then we stand a chance of learning something about the structure of normal science. And that, I hope, puts science and technology studies in a better position to inform policies for science and technology, to better connect with all of the stakeholders in science and technology, to help scientists and engineers organize themselves more effectively on their own terms but also to be more engaged citizens. Ultimately, if we’re still interested in pushing the Kuhnian project forward, then knowing more about what scientists and engineers do all day is fundamental to understanding the structure both of scientific revolutions and of scientific normalcy.