Who Gets Credited, and What “Constructed” Means

Of the 55 Nobel laureates working in the United States in 1963, 34 had studied or collaborated with one of 46 previous prize-winners. And the ones who had worked with a laureate before doing their own important research collected their prizes at an average age of 44, against 53 for everyone else.

Then the question the whole chapter is built on, in Sismondo's own framing. Are those clusters the tip of a merit-based iceberg, or artefacts of a prestige system gone wrong? Is the knowledge elites are recognised for intrinsically valuable, or does it become valuable because of its association with elites?

Two predictions on the record, both wrong. Francis Bacon, in the week 2 packet, thought his inductive method would level the differences between intellects and let science be industrialised: anyone following the procedure would do useful work, because the method does the thinking.

Three hundred years later the Spanish philosopher José Ortega y Gasset said the levelling had happened, and was appalled by it. Science had progressed, he wrote in The Revolt of the Masses (1930), thanks in great part to the work of men astoundingly mediocre, and even less than mediocre. His point was about specialisation. A field cut into small enough pieces can be worked by somebody who knows one piece and nothing else, and that person will still produce results, because the piece is small. Ortega called the type the learned ignoramus: a man who is not ignorant, because he is a scientist, and not learned either, because he knows only his corner, and who is dangerous because his one competence makes him confident everywhere else. So Bacon and Ortega describe the same machine, Bacon as the promise and Ortega as the alarm.

The distributions say otherwise. Roughly 10 per cent of scientific authors produce 50 per cent of all papers. An estimated 80 per cent of citations go to 20 per cent of papers. Science is not flat and it is not a machine that runs on interchangeable operators. Bacon and Ortega are both wrong about its structure.

Every number above is a citation count, so the chapter stops and asks what a citation count measures. The hopeful answer: a citation records an influence. I read your paper, it shaped my work, I cite it, and adding up the citations tells us whose work shaped whose.

Sismondo says that picture is wrong, and the reason is what a paper is for. A paper reads like a report of what happened in the lab, but it is a rational reconstruction: the false starts are dropped, the order of events is rearranged, and the messy history is rewritten as a clean line from question to result. Nobody is lying. The genre simply is not a diary. It is an argument aimed at referees and at the handful of people who will decide whether to believe the result.

Once you see the paper as an argument, the citations become part of the argument. They stop being a record of where the ideas came from. Concretely, that breaks the count in four places:

• You cite what persuades the reader you have in mind. If the referees are in a particular camp, you cite that camp's landmark papers, whether or not you learned anything from them.
• Most of what actually influenced you is uncitable. A technique a postdoc showed you at the bench, an objection somebody raised at a conference, the argument you had with your supervisor: all real influence, none of it has a citable form.
• The most influential work stops being cited at all. Once an idea becomes textbook background, citing it looks naive. Nobody cites Watson and Crick before describing a DNA sequence. Influence so complete that it becomes assumed reads as zero.
• One citation can be doing any of several jobs. Crediting a predecessor, parking a rival's objection, borrowing a method, signalling which literature you belong to, or being cited to be attacked. The count does not distinguish an endorsement from a demolition.

His conclusion is flat: citation analysis is a poor tool for studying communication and influence.

And then he uses the numbers anyway. The justification is size. If the true distribution were mildly uneven, a distorted instrument could easily manufacture the unevenness and you would learn nothing. But 20 per cent of papers holding 80 per cent of citations is not a mild effect, and no amount of rhetorical citing plausibly turns a flat field into that. The instrument is too crude to tell you who influenced whom; it is still good enough to tell you the field is steeply unequal. Notice the move, because you will see it repeatedly in this course: the measure is admitted to be bad, the effect is large enough to survive it, and the author carries on with the caveat on the record.

This is the most useful stretch of the chapter, because it shows one fact supporting two opposite recommendations. The fact both sides accept: 20 per cent of the papers carry 80 per cent of the citations.

Jonathan and Stephen Cole read that as efficiency, and call the lopsided shape a feature. Their reasoning runs in three steps. First, a citation count is at least roughly a value measure, so the 20 per cent really are the papers that mattered. Second, a paper cited once or twice therefore contributed close to nothing, and the money and years that went into it bought close to nothing. Third, even that near-nothing is probably not lost, because important results tend to be found more than once. Calculus arrived twice, natural selection twice, oxygen twice, the telephone in two patent applications on one day. If a finding is ripe, somebody else reaches it within a few years. So the recommendation is concentration: stop spreading grants thinly across everyone and send them to the already-productive people and departments, because that is where the cited work comes from. Funding should track the stratification.

Stephen Turner and Daryl Chubin attack the first step and the whole thing reverses. Suppose citations track visibility, and not worth: a paper by a known name at a known department gets read, cited and built on, while the same result from an unknown department is not read at all. Then the 80 or 20 split is not a map of where the good work is. It is a map of who gets attention, and the uncited majority is good work that was never looked at. Their recommendation is the opposite one: level the playing field, spread support more widely, and cut the effect of prestige and old-boy networks, because the current distribution is not efficiency but waste. The multiples argument cuts their way too: if discoveries really are that ripe, the people who lose the race are competent, and starving them of funding removes the competition that made the discovery arrive quickly at all.

What the disagreement turns on, in Sismondo's words, is how accurate science's system of recognition is. Nobody has an independent measure of a paper's worth to check the citation count against, which is precisely why the same table supports both policies. So the 80 and 20 figure settles nothing by itself. First you have to say what a citation means, and that is the question nobody can answer.

No single variable dominates. One survey builds a portrait of the most productive scientist as someone who is driven, has a strong ego, acts autonomously, plays with ideas, tolerates ambiguity, is at home with abstractions, is detached from non-scientific social relations, reserves mornings for writing, works on routinised problems, is relatively young, went to a prestigious graduate school, had a prestigious mentor, is at a prestigious employer, has freedom to choose problems, has a history of success, and has been cited before.

A later study offers shorter adjectives, in order of importance: persistent, smart, civil, creative, entrepreneurial, aggressive, tasteful, confident, adaptable.

Sismondo's verdict on both lists is worth copying. Many of the items are uncontroversial and none of them is particularly helpful to somebody trying to understand scientific processes. Peak productive years cluster around the mid-forties, and nobody knows why or what would change it. Persistence may matter enormously, and the sources of persistence are unclear. A list of correlates is not an explanation.

One variable does something, though, and it is the one that matters. Scientists at prestigious institutions are strikingly more productive, and institutional prestige is a strong predictor.

The obvious explanation is selection, and the evidence rules it out. Do prestigious departments simply hire people who were going to be more productive anyway? Not in general: the differences in productivity emerge after people have been hired. And it is hard to imagine any hiring committee picking that consistently, in a job market that is almost always tight, between candidates whose potential differs very slightly.

So prestige is doing something. Better facilities. Better networks. More intellectual stimulation. More internal pressure and reward. Or simply more visibility, and therefore more reward for the same work, which Sismondo states as a conclusion with an exclamation mark: if that is right, then prestige by itself makes people's research valuable.

Robert Merton named it after a line in the Gospel of Matthew: to whoever has, more shall be given, and from whoever has not, even what he has shall be taken away.

The mechanism is a chain where each link is small and the compounding is not. Somebody with the traits on those lists is more likely to get a famous mentor. A famous mentor makes a prestigious graduate school more likely. That makes a prestigious department more likely. That brings better facilities, better conversation, and above all more visibility. More visibility means more citations. And citation is itself a reward: people whose work is cited go on publishing. The sociologist Randall Collins calls citations sources of emotional energy.

His framing is that women are worse represented the more elite the grouping, and the figures step down accordingly.

• United States, 2005. Women earned 46 per cent of doctorates in the social sciences, natural sciences and engineering, up from 31 per cent a decade before. But 49 per cent in the biological sciences and 18 per cent in engineering.
• United States, 2006. Only 19 per cent of senior faculty in those areas were women, heavily concentrated in the life and social sciences.
• Europe. Only 15 per cent of senior university faculty across all fields. And the variation between countries is enormous: in 2003 women earned 72 per cent of life science and 45 per cent of physical science doctorates in Italy, against 47 and 23 per cent in Germany. Senior medical faculty: 22 per cent women in the UK, 6 per cent in Germany.
• Japan stands out among large research nations as particularly gendered, with smaller percentages of women researchers of every kind than the United States or any European country.
• And in most countries women are unlikely to be gatekeepers: editors of major journals, chairs of important boards.

The country variation is the part to think about. Italy and Germany are both rich European countries with good universities, and the gap between 72 and 47 per cent has nothing to do with biology. Whatever is producing these numbers travels with the culture.

Margaret Rossiter's history of women scientists in America turns on one finding, and it is counter-intuitive: feminisation is linked to a fall in status, and masculinisation to a rise in it. The direction of causation is from who holds the jobs to how the jobs are regarded.

What that produced, twice. When women began entering scientific fields in the 1860s and 1870s, the men already there perceived that their work was losing its masculine status, and pushed women into marginal positions where they would be invisible. In the twentieth century women found they could enter much more easily through new fields, home economics and nutritional science, where they could do sociology, economics, biology and chemistry under another name. The fields as a whole were then poorly regarded, because they were feminised.

And the sentence in the box that people quote. Women's colleges had been a safe place for women scientists to work and build credentials. After the Second World War, as American universities expanded, those colleges and the less prestigious universities followed the leading ones in hiring more men. The golden age of American science after the war was a dark age for women in it.

What changed it was not science. The shift came in the 1960s, from outside: the National Organization for Women, Betty Friedan, and Alice Rossi's 1965 article in Science titled "Women in Science: Why So Few?", which made the case that science was no different from any other profession. Alongside that ran a legal revolution producing anti-discrimination law and affirmative action, which women then used as resources to get in.

The standard metaphor is Natalie Angier's. Women flow through a pipe with leaks at every joint along its span, a pipe that begins with a high-pressure surge of young women at the source, a roiling Amazon of smart graduate students, and ends at the spigot with a trickle of women prominent enough to be deans or department heads or to win a Nobel Prize.

His objection is that the picture makes the problem one of leakage, which puts all the attention at the joints and none at either end. The metaphor only works if you also attend to intake, blockage and filters: processes of inclusion and exclusion. In many fields there is no roiling Amazon at the source to begin with, and the women who are there do not simply leak out, they are discouraged the whole way along.

The framing he prefers is Sara Delamont's three problems, and they are the three sub-headings of the rest of the chapter: getting in, staying in, and getting on.

Science and engineering have masculine images and the stereotypical scientist is male, and that shapes what girls believe about their own capacity. Quite young girls may find it hard to think of themselves as potential scientists, and in many environments they are actively discouraged by teachers, peers and parents. The consequence is structural and not merely attitudinal: by the end of secondary school many girls who might have been interested already lack the background subjects they would need to study science at university. The door closes before anybody applies.

The concept to take from this section is the unofficial PhD programme. Alongside the official courses, exams and research there runs a second curriculum: study groups, pick-up basketball, informal mentoring, and simply the ongoing conversation and consultation of a department. Even a well-integrated student can be shut out of parts of it.

Then the hardest number in the chapter. A study of peer review scores for postdoctoral fellowships at the Swedish Medical Research Council found reviewers rating men's accomplishments as overwhelmingly more valuable than apparently equivalent accomplishments by women. To be given the same competence score as a male colleague, a woman needed to exceed his scientific productivity by about three extra papers in Nature or Science, or twenty extra papers in an excellent specialist journal.

And a clash of clocks. Shirley Tilghman, a molecular biologist and later president of Princeton, argues that the pressure at the start of a career falls hardest on women. Research productivity decides whether a senior graduate student or postdoc gets a permanent job, and new faculty then have about six years to clear an all-or-nothing tenure hurdle. Those are exactly the years in which women are most likely to want to have children.

The discriminations at this stage are individually small enough to argue about. Women hired at the same time as male peers tend to have smaller laboratories, and to have negotiated worse arrangements for start-up grants, for the overhead the university takes from their research money, for salary and for teaching load.

And they remain outside the informal networks. Inside their departments they tend not to have informal mentors to steer them through opaque processes. Outside them they do less collaborative research. And they are less well connected to the networks that carry unpublished work, which leaves them more dependent on the published literature and therefore always slightly behind. Sismondo quotes Jonathan Cole's formulation: women have moved into science, but they are not of the community of science.

Which is where the Matthew Effect returns and does the argument's real work. In any individual case these differences look trivial, and a woman may well shrug them off. But if competition is strong enough, and if advantage compounds, the small irritants are enough on their own to keep her from getting on. No single act of discrimination has to be large.

One side claims a biological propensity. Claims of a maths gene or something like it go back to 1980, and as recently as 2005 the president of Harvard, Lawrence Summers, invoked biology to explain differences in men's and women's success in science and engineering.

Sismondo's reply is two lines and both are worth having. First, genes only act in environments. A gene does nothing on its own. Whether it is switched on, and how strongly, depends on what surrounds it: food, hormones, how a child is taught, what a child is praised for trying. So there is no way to measure what a gene does apart from a setting, and saying a difference is genetic is a way of calling it fixed without having shown it is. Second, the scores are moving. Boys' and girls' mathematics results have been getting closer, and genes have not changed in thirty years, so whatever was making the gap was in the setting.

The other side claims a difference in style, and he reports it without endorsing it. A number of feminists and non-feminists have argued that women tend to think in more concrete terms, are better served by problem-centred learning, think more relationally, and produce more holistic pictures. He parks the whole question for chapter 7, which is weeks 5 to 7 of this course. The question there is whether who is doing the knowing changes what gets known. The name for that field is feminist epistemology, and epistemology on its own means the study of knowledge: what knowing is, and what makes one claim better than another.

Cumulative advantage is what makes the argument work. Point at any single thing on the list, a smaller lab, a worse starting salary, being left out of the conversation about the drying agent, and it looks too small to end a career. None of them on its own pushes a woman out. The claim is that they add up: a smaller lab means fewer results, fewer results mean a weaker grant, a weaker grant means a smaller lab again. Five years of that is a gap nobody can close. It also explains why two women can describe completely different careers and still be describing the same pattern, because the list is long and each person meets a different few items on it.

Then the sentence the chapter title has been leading to. Once you add the discrimination section to the funding section, it is hard to call science efficient at all, because it is throwing away the work of half the people it trained. It looks less like an efficient meritocracy and more like an inefficient old boys' network, in which people and ideas become important partly because of where they sit in a social network.

And the claim that connects this chapter to the next one. Elite groups are socially constructed: the ranking was built by people and it could have come out differently. He grants straight away that elites really do produce more and better work, because they have the money, the labs and the encouragement. Then he asks the question he opened the chapter with and leaves it open:

• Is famous work important, or is it called important because a famous person did it? The same result signed by a Harvard lab and by an unknown one gets read differently, and Sismondo has no way to tell how much of the difference is the work.
• Would science look different if the rewards were spread evenly? If prestige is part of what makes work count, then flattening it would change which results get taken up, and therefore what science ends up believing.

Start with the problem, because the chapter does not. People say that is socially constructed about money, about gender, about quarks and about the number of planets, and they mean wildly different things by it. Sometimes it means something nobody would argue with: a twenty dollar bill is worth twenty dollars because we all treat it that way, and if we stopped it would be paper. Sometimes it means something enormous: that there is no fact about whether atoms exist apart from what scientists agreed to say. Same three words, and the two claims have almost nothing in common.

So arguments about social construction mostly go nowhere. One person defends the twenty dollar bill version. The other attacks the atoms version. They both leave convinced the other is an idiot. Sismondo's job in this chapter is to stop that from happening: he takes the phrase apart into seven separate claims, arranged from the one nobody can deny to the one he himself rejects, so that you can point at a sentence and say which claim is actually being made.

Why you need it. Weeks 5 to 9 of this course are feminist epistemology and the philosophy of disability, and both run on the word constructed. If you cannot say which of the seven a given author means, none of it will make sense. And this is the obvious short-answer question: what does it mean to say something is socially constructed.

The phrase arrived in the field in the late 1970s and then went everywhere. Books have claimed to show the construction of facts, of knowledge, of theories, of phenomena, of science, of technologies, of societies. It became the label holding a lot of different work together, and the target of fierce attacks from historians, philosophers and sociologists, usually fighting under the banner of realism.

Sismondo's move is to refuse to defend or attack it, and to take it apart instead. Ian Hacking, writing on constructivism in 1999, had gone the other way and built the strongest possible version of it, to set against realism. His version has three parts, and each has a technical name you will meet again:

• This theory was not the only one that could have won. It could have gone another way. The word for that is contingency.
• The boxes a theory sorts things into were drawn by people. Nature does not come with labels on it. The word for that is nominalism.
• The reason everyone still believes it has little to do with how good the evidence is. Something outside the evidence is holding it in place. The name for that is an external explanation.

Hacking built that to give realism something solid to hit.

Sismondo pulls the phrase into seven separate claims instead. Some are plainly anti-realist. Some are not. Several are so obviously true that a realist has to accept them. That is what the chapter is for, and it is why she set it.

What all seven have in common is three reminders: that science and technology are social; that they are active, which is what the building metaphor is for; and that they do not run in a straight line from nature to ideas about nature, so their products are not themselves natural.

Where the phrase came from. STS took it from Peter Berger and Thomas Luckmann's The Social Construction of Reality of 1966, a book about the sociology of knowledge. Their subject is social reality: the institutions and structures that exist because enough people behave as though they do.

Their conditions are worth having exactly, because they are a recipe. To construct an X you need only three things. That knowledge of X encourages behaviour which makes other people more or less likely to act as though X exists. That knowledge of X is reasonably common. And that knowledge of X gets passed on. Given those, X cannot be wished away, and so it exists.

What it means for science. Knowledge, methods, disciplinary boundaries and styles of work are all real in this same way, and contingently real.

Contingently real means real, and it did not have to be. Both halves matter. Real, because it has teeth: peer review decides who gets hired and which results count, and you cannot opt out of it. Contingent, because it could have been otherwise and nearly was: peer review in its current form barely existed before the middle of the twentieth century, and nothing in nature required it. So calling it contingent is not calling it fake. It means that if the history had gone differently, this thing would be different, and if people stopped doing it tomorrow it would stop existing, which is not true of an electron.

How you can tell a fact is socially real: push on it and see whether it pushes back. This is Ludwik Fleck, in 1935. Write a paper that ignores something everyone in your field takes for granted, and you will not get a debate. You will get referees rejecting it, colleagues declining to cite you and a grant panel passing you over. The fact is built into the journals, the funding and the hiring, so it stops you the way a wall stops you. That resistance is the thing Sismondo means by the fact's social reality.

And it is the same test as the one used on gender a moment ago: a thing is real when it has causal powers, meaning when it makes a difference to what happens to you. Fleck is worth the name, because his 1935 book on how a scientific fact comes into being is the one Kuhn credits in the preface to Structure, which is last week's reading.

And the sentence that stops this being a criticism. That solidity is what makes science able to move at all.

Imagine the alternative. Every paper you write has to first re-establish that DNA carries heredity, that the balance in the lab is accurate, that oxygen exists. Nobody would get past the first page, and nothing would ever accumulate. Science gets anywhere because almost everything is settled and nobody reopens it, which is exactly the resistance Fleck described. So the thing that looks like conformity from outside is the reason there is anything to build on. Sismondo puts it in early because readers hear socially constructed as an accusation, and here the social part is doing the useful work.

The active version. Latour and Woolgar tracked one statement about a hormone through the literature as it moved from near-nonsense, to possible, to false, to possibly true, to a solid fact, and catalogued what can be done to a paper along the way: ignore it, cite it approvingly, cite it dismissively, question it strongly or weakly, and finally ignore it again because everyone accepts it. Facts are constructed by scientists, one operation at a time, and never by science in the abstract.

The general problem: it is hard to say when a discovery happened. Was oxygen discovered when Priestley made a pure sample of it, when Lavoisier explained what it was, or later still when somebody gave an account that matches ours? Augustine Brannigan's answer is an attributional model: discoveries are not events in themselves, they are events retrospectively recognised as origins.

How he became the discoverer, which is a story about a priority dispute and hardly at all about peas. Hugo de Vries had read Mendel before 1900, and the first of his three papers on his own results does not mention him. Carl Correns read de Vries's first paper, realised he had lost the race, and quickly published his own work labelling the finding "Mendel's Law". Having lost priority to a living rival, he assigned it to a dead man instead. De Vries's later papers accept Mendel's priority in awkward afterthoughts and grumble about the obscurity of the journal.

And Sismondo's line. Had Correns read one or two generations further back, the title could have gone to any of several people. Mendel discovered his laws in 1866, but only as a result of the events of 1900.

This is the sense he calls the most novel, and its subject is objects. Many of the things scientists study are not natural things.

Karin Knorr Cetina's formulation: nature is not to be found in the laboratory. To an outside observer the laboratory shows itself as a place from which nature has been excluded as far as possible.

The evidence is completely ordinary, and that is why it is hard to argue with. The materials arrive already prepared: chemists buy purified reagents, geneticists use established DNA libraries, biologists use engineered animal models. Once inside, the objects are put in artificial situations to see how they react, and subjected to what Latour calls trials of strength. And at best scientists create phenomena, new stable objects of study that did not previously occur. Hacking's version: most of the phenomena of modern physics are manufactured.

So laboratory knowledge is knowledge about distinctly non-natural things, built by hands-on material work.

And the asymmetry he points out is worth keeping. For technology none of this is the least bit surprising. Technology is expected to give new shape to old materials and leave nature behind. The claim only sounds radical when it is made about science, because science is presumed to display the forms of nature exactly as they are.

The easiest of the seven: science and technology change the world, and changing the world is building it.

Technology, intended and not. The success of the petrol car helped create the suburb and the suburban way of living, and to the extent that manufacturers worked to grow the suburban market, that was deliberate. Computers, programs and networks are designed with their social effects in view: dispersed work, control at a distance, or straight military power.

Science too, and his example is pointed. Research into the causes of gender difference has the effect of naturalising those differences. There is great public appetite for it, so work on genes, hormones and brain differences between men and women is well reported, and more often than not reported to emphasise how inevitable stereotypical behaviour is. There is good reason to expect that the reporting has effects on gender itself, which loops straight back to sense 1.

And policy. Government action is increasingly held accountable to scientific evidence, to the point where almost nothing in health, the economy, the environment or defence can be done unless it can be claimed that a study supports it. Studies shape policies, and policies shape the material and social world.

The claim in one line: the data never picks the theory for you.

Think of points on a graph. You have twenty measurements plotted. How many curves pass through all twenty points? Infinitely many. Drawing one of them is a choice, and the points did not make it. That is what Sismondo means by calling science constructive in a geometrical sense: you build a shape that fits the fixed points, and the fixed points are never enough to fix the shape.

A real case you already have. Ptolemy puts the earth at the centre with circles on circles. Copernicus puts the sun at the centre. For a century both predicted where Mars would appear about equally well. Same sky, same observations, two incompatible pictures. If you want to choose, you have to bring in something the observations do not contain: what counts as a simple explanation, what God would plausibly have done, what your instruments can be made to do, what your colleagues will accept. All of those come from people, and that is the sense in which a theory is built and not read off.

Here is the surprise: the pro-science philosophers say this too. You would expect this claim from someone hostile to science. But it is roughly the position of the group from week 2 who held that a sentence means nothing at all unless you could either check it by observation or work it out by logic, so that everything untestable had to go and science could stay. They were about as pro-science as anyone has ever been. They are the Vienna Circle, and the position is called logical positivism. They accepted that for any good theory you can build rivals that account for the data just as well. Bas van Fraassen, their modern heir, says it in the plainest terms: scientific activity is construction and never discovery. Scientists build models that have to match what can be observed, and they do not discover truths about the parts you cannot see.

Where Sismondo and the positivists part company. The positivists thought the problem mostly went away once you fixed the logical framework: settle the rules first, and working inside them is close to mechanical. Sismondo says no framework does that much work, and the reason is old. Going from particular cases to a general rule is always a leap: every swan I have seen is white, so all swans are white. No number of cases makes the rule certain, and no procedure carries you from a finite pile of measurements to the right general theory. That leap is called induction, and the gap in it is the problem of induction. The gap is always there.

So what fills the gap? Karin Knorr Cetina watched scientists to find out, and her answer is a list of ordinary things: the practices already established in the lab, decisions made years earlier for reasons nobody remembers, concepts borrowed from elsewhere and stretched to a new job, tinkering, and local accidents. Which is why two labs can face the same data and end up in different places.

And the line that sums the section up: representations of nature are connected to nature, and they do not necessarily correspond to it in any strong sense.

What that distinction means. Take a metro map. It is connected to the real tunnels, it is built from surveys of them, and it will get you where you are going. It is also geometrically false: the distances are wrong, the angles are wrong, the curves are straightened. Connected, useful, and not a picture of the thing. That is the position on theories, and it is why the section is genuinely arguable.

The term to learn here is heterogeneous engineering, from John Law. An entrepreneurial engineer faces technical, social and economic problems at once and has to bind the solutions into a configuration that works. So they are simultaneously producing knowledge, social realities, and material things, and the constructions can be separated on paper and not in practice.

The strong version of the claim: builders of technology have to build the artefact and build the environment in which the artefact can function, and neither job can usually be done alone. They must combine raw materials, skills, knowledge and capital, which means enrolling a lot of actors who are not all immediately compatible.

And scientific work is the same. Actor-network theory treats scientists and engineers as separated only by disciplinary boundaries. Both build networks, the larger and more stable the better, out of laboratory equipment, established knowledge, patrons, money and institutions. No one piece of a network can determine the shape of the whole.

The word for the general case is co-production, and his examples are good ones. The criteria for good climate science are shaped by policy concerns while the criteria for good policy are shaped by climate science. Ideas about health and disease bend around standardised classifications of diseases and interventions. Assisted reproduction looks miraculous and works through mundane work integrating political, legal, ethical, bureaucratic, medical, technical and intensely personal domains at once.

An old philosophical fight, imported. Are natural kinds part of the world, or only part of our classifying? The traditional version is about universals, the abstractions that range over individual things, like redness.

• Nominalists hold that kinds are human impositions, even where classifying is easy and everyone agrees. Only individual objects are real. Their difficulty with the other view: where would a general property exist, and how would it attach to an object?
• Realists hold that kinds are real features of the world, even where their edges are fuzzy and their application partly conventional. Their difficulty with the other view: do we not discover features of the world, and if kinds were not real, why would classifying be worth anything?

Nominalism is one way of cashing out the construction metaphor. If kinds are not features of the world then they are made, and if they are made by groups of people then they are socially made.

And then the sentence that earns the chapter its place in this course. Since science is the most influential institution that classifies things, science is central to the social construction of reality. Deciding what counts as a species, a disease, a planet or a race is deciding what there is.

It is a short step from nominalism to the strongest claim in the field, and Sismondo takes the step and then refuses it. On this version, representations directly shape their objects: when scientists agree on a claim, they literally make it true. The world comes to match the agreement, with the arrow of dependence pointing that way. When engineers agree on the most efficient solution, that makes it the most efficient one.

He calls it neo-Kantian constructivism, because Kant held that human beings impose some structures on the world, and this is that with a social mind in place of an individual one.

Two things make it plausible, and they are not stupid.

• There is no independent access. The natures of things are never available without a representation. When anyone agrees about anything they do so in response to sense experience, mediated information and arguments, and even sense experience is itself a response to something.
• Contingency before stability. Close studies of science find a great deal of contingency in knowledge before it settles. Disagreement is the rule and not the exception. Yet objects behave themselves once agreement is reached, and that change needs explaining.

Steve Woolgar states the position most directly, arguing that the existence and character of a discovered object differ according to the social network, that the network does not merely mediate between the object and the observation but constitutes the object, and that the relationship therefore inverts: the representation gives rise to the object.

Sismondo's objection is a question about mechanism, and it is devastating precisely because it is simple. Kant's version was modest because it was individual: a person imposes structure as they apprehend the world, and there is nothing to explain. STS cannot be modest in that way, because its whole emphasis is social. So: how does consensus affect material reality? How do the convictions of authorities carry weight with the world that the convictions of non-authorities do not? How does agreement cause a change in matter?

If it were true, representation would act at a distance with no mediators. A successful representation would change or create the thing it represents, with no causal connection running from one to the other. That violates fundamental assumptions about cause and effect, and it is why Latour says social constructivism is not plausible for more than a second.

Then a political objection, and it is the one worth carrying into a seminar. Feminists point out that science's images of women are sometimes sexist, especially in how fast they naturalise gender. If neo-Kantian constructivism were right, a feminist critic could try to change science's construction of women but could not call it false, because scientific consensus would be true by definition. The same trap catches environmentalists: they could argue about the dominant view of how resilient nature is, and never say it was wrong. The strongest form of the constructivist claim disarms exactly the people who most want to use it.

And then he half gives it back. Given that several of the other six senses are obviously true, neo-Kantian constructivism may be a decent approximation and methodologically useful even if it is wrong as metaphysics. Talk about the social construction of reality may amount to little more than metaphor or sweeping language, and as a metaphor it does a job: it draws attention to contingency, and sends researchers off to ask what caused it.

The phrase escaped the field. Construction talk is now used in psychology, geography, environmental studies, education, management, cultural studies and even accounting, and STS is partly responsible: because scientific knowledge is normally taken to reflect the natural world with scientists as passive conduits, saying that scientific realities are constructed was a genuinely radical claim, and radical claims travel.

But the diversity means there is no neat theory there. What survives is the three reminders: science and technology are social, they are active, and they do not take nature as it comes.

And the closing position, which is the thing to quote if anyone accuses this field of relativism. Some of these forms are controversial in principle and all are controversial in application, but given their diversity even the staunchest realist cannot dismiss constructivist claims out of hand. Constructivism is the study of how scientists and technologists build socially situated knowledge and things, and such studies can show how scientists build good representations of the material world, in a perfectly ordinary sense.

He then says where science's power comes from, in his own voice: its ability to manipulate nature and measure nature's reactions, and its ability to carry those measurements across time and space to other laboratories and other contexts. Laboratory technologies contribute to objectivity and to objective knowledge.

So constructivist STS may even support a version of realism. Not the idea that anybody has unmediated knowledge of reality, and not the idea that there is one complete set of truths. But a version.