## 1. Historical Background



Philosophers who study the social character of scientific knowledge
can trace their lineage at least as far as John Stuart Mill. Mill,
Charles Sanders Peirce, and Karl Popper all took some type of critical
interaction among persons as central to the validation of knowledge
claims.



Mill's arguments occur in his well-known political essay On
Liberty, (Mill 1859) rather than in the context of his logical and
methodological writings, but he makes it clear that they are to apply
to any kind of knowledge or truth claim. Mill argues from the
fallibility of human knowers to the necessity of unobstructed
opportunity for and practice of the critical discussion of ideas. Only
such critical discussion can assure us of the justifiability of the
(true) beliefs we do have and can help us avoid falsity or the
partiality of belief or opinion framed in the context of just one
point of view. Critical interaction maintains the freshness of our
reasons and is instrumental in the improvement of both the content and
the reasons of our beliefs. The achievement of knowledge, then, is a
social or collective, not an individual, matter.



Peirce's contribution to the social epistemology of science is
commonly taken to be his consensual theory of truth: "The
opinion which is fated to be ultimately agreed to by all who
investigate is what we mean by truth, and the object represented is
the real." (Peirce 1878, 133) While often read as meaning that
the truth is whatever the community of inquirers converges on in the
long run, the notion is interpretable as meaning more precisely either
that truth (and "the real") depends on the agreement of
the community of inquirers or that it is an effect of the real that it
will in the end produce agreement among inquirers. Whatever the
correct reading of this particular statement, Peirce elsewhere makes
it clear that, in his view, truth is both attainable and beyond the
reach of any individual. "We individually cannot hope to attain
the ultimate philosophy which we pursue; we can only seek it for the
community of philosophers." (Peirce 1868, 40). Peirce puts great
stock in instigating doubt and critical interaction as means to
knowledge. Thus, whether his theory of truth is consensualist or
realist, his view of the practices by which we attain it grants a
central place to dialogue and social interaction.



Popper is often treated as a precursor of social epistemology because
of his emphasis on the importance of criticism in the development of
scientific knowledge. Two concepts of criticism are found in his works
(Popper 1963, 1972) and these can be described as logical and
practical senses of falsification. The logical sense of falsification
is just the structure of a modus tollens argument, in which a
hypothesis is falsified by the demonstration that one of its logical
consequences is false. This is one notion of criticism, but it is a
matter of formal relations between statements. The practical sense of
falsification refers to the efforts of scientists to demonstrate the
inadequacies of one another's theories by demonstrating
observational shortcomings or conceptual inconsistencies. This is a
social activity. For Popper the methodology of science is
falsificationist in both its logical and practical senses, and science
progresses through the demonstration by falsification of the
untenability of theories and hypotheses. Popper's logical
falsificationism is part of an effort to demarcate genuine science
from pseudo science, and has lost its plausibility as a description of
scientific methodology as the demarcation project has come under
challenge from naturalist and historicist approaches in philosophy of
science. While criticism does play an important role in some current
approaches in social epistemology, Popper's own views are more
closely approximated by evolutionary epistemology, especially that
version that treats cognitive progress as the effect of selection
against incorrect theories and hypotheses. In contrast to Mill's
views, for Popper the function of criticism is to eliminate false
theories rather than to improve them.



The work of Mill, Peirce, and Popper is a resource for philosophers
presently exploring the social dimensions of scientific knowledge.
However, the current debates are framed in the context of developments
in both philosophy of science and in history and social studies of
science following the collapse of the logical empiricist consensus.
The philosophers of the Vienna Circle are conventionally associated
with an uncritical form of positivism and with the logical empiricism
that replaced American pragmatism in the 1940s and 1950s. According to
some recent scholars, however, they saw natural science as a potent
force for progressive social change. (Cartwright, Cat, and Chang 1996;
Giere and Richardson, eds., 1996; Uebel 2005) With its grounding in
observation and public forms of verification, science for them
constituted a superior alternative to what they saw as metaphysical
obscurantism, an obscurantism that led not only to bad thinking but to
bad politics. While one development of this point of view leads to
scientism, the view that any meaningful question can be answered by
the methods of science; another development leads to inquiry into what
social conditions promote the growth of scientific knowledge. Logical
empiricism, the version of Vienna Circle philosophy that developed in
the United States, focused on logical, internal aspects of scientific
knowledge and discouraged philosophical inquiry into the social
dimensions of science. These came into prominence again after the
publication of Thomas Kuhn's *Structure of Scientific
Revolutions* (Kuhn 1962). A new generation of sociologists of
science, among them Barry Barnes, Steven Shapin, and Harry Collins,
took Kuhn's emphasis on the role of non-evidential community
factors in scientific change even further than he had and argued that
scientific judgment was determined by social factors, such as
professional interests and political ideologies (Barnes 1977, Shapin
1982, Collins 1983). This family of positions provoked a
counter-response among philosophers. These responses are marked by an
effort to acknowledge some social dimensions to scientific knowledge
while at the same time maintaining its epistemological legitimacy,
which they take to be undermined by the new sociology. At the same
time, features of the organization of scientific inquiry compel
philosophers to consider their implications for the normative analysis
of scientific practices.


## 2. Big Science, Trust, and Authority



The second half of the twentieth century saw the emergence of what has
come to be known as Big Science: the organization of large numbers of
scientists bringing different bodies of expertise to a common research
project. The original model was the Manhattan Project, undertaken
during the Second World War to develop an atomic weapon in the United
States. Theoretical and experimental physicists located at various
sites across the country, though principally at Los Alamos, New
Mexico, worked on sub-problems of the project under the overall
direction of J. Robert Oppenheimer. While academic and military
research have since been to some degree separated, much experimental
research in physics, especially high energy particle physics,
continues to be pursued by large teams of researchers. Research in
other areas of science as well, for example the work comprehended
under the umbrella of the Human Genome Project, has taken on some of
the properties of Big Science, requiring multiple forms of expertise.
In addition to the emergence of Big Science, the transition from small
scale university or even amateur science to institutionalized research
with major economic impacts supported by national funding bodies and
connected across international borders has seemed to call for new
ethical and epistemological thinking. Moreover, the consequent
dependence of research on central funding bodies and increasingly,
private foundations or commercial entities, prompts questions about
the degree of independence of contemporary scientific knowledge from
its social and economic context.



John Hardwig (1985) articulated one philosophical dilemma posed by
large teams of researchers. Each member or subgroup participating in
such a project is required because each has a crucial bit of expertise
not possessed by any other member or subgroup. This may be knowledge
of a part of the instrumentation, the ability to perform a certain
kind of calculation, the ability to make a certain kind of measurement
or observation. The other members are not in a position to evaluate
the results of other members' work, and hence, all must take one
anothers' results on trust. The consequence is an experimental
result, (for example, the measurement of a property such as the decay
rate or spin of a given particle) the evidence for which is not fully
understood by any single participant in the experiment. This leads
Hardwig to ask two questions, one about the evidential status of
testimony, and one about the nature of the knowing subject in these
cases. With respect to the latter, Hardwig says that either the group
as a whole, but no single member, knows or it is possible to know
vicariously. Neither of these is palatable to him. Talking about the
group or the community knowing smacks of superorganisms and
transcendent entities and Hardwig shrinks from that solution.
Vicarious knowledge, knowing without oneself possessing the evidence
for the truth of what one knows, requires, according to Hardwig, too
much of a departure from our ordinary concepts of knowledge.



The first question is, as Hardwig notes, part of a more general
discussion about the epistemic value of testimony. Much of what passes
for common knowledge is acquired from others. We depend on experts to
tell us what is wrong or right with our appliances, our cars, our
bodies. Indeed, much of what we later come to know depends on what we
previously learned as children from our parents and teachers. We
acquire knowledge of the world through the institutions of education,
journalism, and scientific inquiry. Philosophers disagree about the
status of beliefs acquired in this way. Here is the question: If
*A* knows that *p* on the basis of evidence *e*,
*B* has reason to think *A* trustworthy and *B*
believes *p* on the basis of *A*'s testimony that
*p*, does *B* also know that *p*? Some
philosophers, as Locke and Hume seem to have, argue that only what one
has observed oneself could count as a good reason for belief, and that
the testimony of another is, therefore, never on its own sufficient
warrant for belief. Thus, *B* does not know simply on the basis
of *A*'s testimony but must have additional evidence
about *A*'s reliability. While this result is consistent
with traditional philosophical empiricism and rationalism, which
emphasized the individual's sense experience or rational
apprehension as foundations of knowledge, it does have the consequence
that we do not know most of what we think we know.



A number of philosophers have recently offered alternative analyses
focusing on one or another element in the problem. Some argue that
testimony by a qualified expert is itself evidential, (Schmitt 1988),
others that the expert's evidence constitutes good reason for,
but is not itself evidential for the recipient of testimony (Hardwig
1985, 1988), others that what is transmitted in testimony is knowledge
and not just propositional content and thus the question of the kind
of reason a recipient of testimony has is not to the point (Welbourne
1981).



However this dispute is resolved, questions of trust and authority
arise in a particularly pointed way in the sciences, and
Hardwig's dilemma for the physics experiment is also a specific
version of a more general phenomenon. A popular conception of science,
fed partly by Popper's falsificationism, is that it is
epistemically reliable because the results of experiments and
observational studies are checked by independent repetition. In
practice, however, only some results are so checked and many are
simply accepted on trust. Not only must positive results be accepted
on trust, but claims of failure to replicate as well as other
critiques must be also. Thus, just as in the non-scientific world
information is accepted on trust, so in science, knowledge grows by
depending on the testimony of others. What are the implications of
accepting this fact for our conceptions of the reliability of
scientific knowledge?



The philosopher of biology, David Hull, argued in his (1988) that
because the overall structure of reward and punishment in the sciences
is a powerful incentive not to cheat, further epistemological analysis
of the sciences is unnecessary. What scientists have to lose is their
reputation, which is crucial to their access to grants,
collaborations, prizes, etc. So the structure itself guarantees the
veridicality of research reports. But some celebrated recent episodes,
such as the purported production of "cold fusion" were
characterized by the failure of replication attempts to produce the
same phenomenon. And, while the advocates of cold fusion were
convinced that their experiments had produced the phenomenon, there
have also been cases of outright fraud. Thus, even if the structure of
reward and punishment is an incentive not to cheat, it does not
guarantee the veridicality of every research report.



On Hull's view, the scientific community seeks true theories or
adequate models. Credit, or recognition, accrues to individuals to the
extent they are perceived as having contributed to that community
goal. That is, individual scientists seek reputation and recognition,
to have their work cited as important and as necessary to further
scientific progress. Cheating, by misreporting experimental results or
other misconduct, will be punished by loss of reputation. But this
depends on strong guarantees of detection. Absent such guarantees,
there is as strong an incentive to cheat, to try to obtain credit
without necessarily having done the work, as not to cheat.



Both Alvin Goldman (Goldman, 1995, 1999) and Philip Kitcher (1993)
have treated the potential for premature, or otherwise (improperly)
interested reporting of results to corrupt the sciences as a question
to be answered by means of decision theoretic models. The decision
theoretic approach to problems of trust and authority treats both
credit and truth as utilities. The challenge then is to devise
formulas that show that actions designed to maximize credit also
maximize truth. Kitcher, in particular, develops formulas intended to
show that even in situations peopled by non-epistemically motivated
individuals (that is, individuals motivated more by a desire for
credit than by a desire for truth), the reward structure of the
community can be organized in such a way as to maximize truth and
foster scientific progress. One consequence of this approach is to
treat scientific fraud and value or interest infused science as the
same problem. One advantage is that it incorporates the motivation to
cheat into the solution to the problem of cheating. But one may wonder
how effective this solution really is. Increasingly, we learn of
problematic behavior in science based industries, such as the
pharmaceutical industry. Results are withheld or distorted, authorship
is manipulated. Hot areas, such as stem cell research, cloning, or
gene modification, have been subjected to fraudulent research. Thus,
even if the structure of reward and punishment is an in principle
incentive not to cheat, it does not guarantee the reliability of every
research report. The decision theoretic model needs to include at
least one more parameter, namely the anticipated likelihood of
detection within a relevant timeframe.



Community issues have also been addressed under the banners of
research ethics and of peer review. One might think that the only
ethical requirements on scientists are to protect their research
subjects from harm and, as professional scientists, to seek truth
above any other goals. This presupposes that seeking truth is a
sufficient guide to scientific decision-making. Heather Douglas, in
her critical study of the ideal of value-freedom (Douglas 2009),
rejects this notion. Douglas draws on her earlier study of inductive
risk (Douglas 2000) to press the point that countless methodological
decisions required in the course of carrying out a single piece of
research are underdetermined by the factual elements of the situation
and must be guided by an assessment of the consequences of being
wrong. Science is not value-free, but can be protected from the
deleterious effects of values if scientists take steps to mitigate the
influence of inappropriate values. One step is to distinguish between
direct and indirect roles of values; another is the articulation of
guidelines for individual scientists. Values play a direct role when
they provide direct motivation to accept or reject a theory; they play
an indirect role when they play a role in evaluating the consequences
of accepting or rejecting a claim, thus influencing what will count as
sufficient evidence to accept or reject. The responsibility of
scientists is to make sure that values do not play a direct role in
their work and to be transparent about the indirect roles of values. A
number of writers have taken issue with the tenability of
Douglas's distinction between direct and indirect. Steel and
Whyte (2012) examine testing guidelines developed by pharmaceutical
companies to point out that the very same decision may be motivated by
values playing a direct role or playing an indirect role. If the point
is to prohibit practices such as withholding negative results, then it
shouldn't matter whether the practice is motivated by values
functioning directly or indirectly. Elliott (2011) questions whether
only harmful consequences should be considered. If science is to be
useful to policy makers, then questions of relative social benefit
should also be permitted to play a role. Finally the cognitive
activities demanded by Douglas's ethical prescriptions for
scientists seem beyond the capacities of individual scientists. This
point will be pursued below.



Torsten Wilholt (2013) argues that the research situation is more
complicated than the epistemic vs. nonepistemic tradeoff implied by
the decision theoretic approach. In part because of the difficulties
in achieving the degree of knowledge required to realize
Douglas's ethical prescriptions, he argues that the reliance
called for in science extends beyond the veridicality of reported
results to the values guiding the investigators relied upon. Most
research involves both results expressed statistically (which requires
choice of significance threshold and balancing chances of Type I vs.
Type II error) and multiple steps each requiring methodological
decisions. These decisions, Wilholt argues, represent trade-offs among
the reliability of positive results, the reliability of negative
results, and the power of the investigation. In making these
tradeoffs, the investigator is per force guided by an evaluation of
the consequences of the various possible outcomes of the study.
Wilholt extends the arguments about inductive risk offered originally
by Richard Rudner and elaborated by Heather Douglas to propose that,
in relying on another's results I am relying not only on their
competence and truthfulness, but on their making methodological
decisions informed by the same valuations of outcomes as I have. This
attitude is more than epistemic reliance, but a deeper attitude: one
of trust that we are guided by the same values in a shared enterprise.
For Wilholt, then, scientific inquiry engages ethical norms as well as
epistemic norms. Formal or mechanical solutions such as those
suggested by the application of decision theoretic models are not
sufficient, if the community must be held together by shared ethical
values.



Peer review and replication are methods the scientific community,
indeed the research world in general, employs to assure consumers of
scientific research that the work is credible. Peer review both of
research proposals and of research reports submitted for publication
screens for quality, which includes methodological competence and
appropriateness as well as for originality and significance, while
replication is intended to probe the robustness of results when
reported experiments are carried out in different laboratories and
with slight changes to experimental conditions. Scholars of peer
review have noted various forms of bias entering into the peer review
process. In a review of the literature, Lee, Sugimoto, Zhang, and
Cronin (2013) report documented bias along gender, language,
nationality, prestige, and content as well as such problems as lack of
inter-reviewer reliability consistency, confirmation bias, and
reviewer conservatism. Lee (2012) argues that a Kuhnian perspective on
values in science interprets lack of inter-reviewer consistency as
variation in interpretation, applicability, and weight assigned to
shared values by different members of the scientific community. Lee
and colleagues (2013) argue that journal editors must take much more
action than is currently taken to require that researchers make their
raw data and other relevant trial information available to enable peer
reviewers to conduct their work adequately.



One issue that has yet to be addressed by philosophers is the gap
between the ideal of replication resulting in confirmation,
modification, or retraction and the reality. This ideal lies behind
the assumptions of efficacy of structures of reward and sanction. Only
if researchers believe that their research reports will be probed by
efforts at replication will the threat of sanctions against faulty or
fraudulent research be realistic. John Ioannidis and collaborators
(Tatsioni, Bonitsis, and Ioannidis 2007; Young, N.S. Ioannidis, and
Al-Ubaydli 2008) have shown how infrequently attempts to replicate are
actually made and, even more strikingly, how contradicted results
persist in the literature. This is an issue that goes beyond
individuals and beyond large research collaborators to the scientific
community in general. It underscores Wilholt's contention that
the scientific community must be held together by bonds of trust, but
much more empirical and philosophical work is needed to address how to
proceed when such trust is not justified. The demonstration of
widespread lack of replicability on studies in psychology and in
biomedical research has prompted debate about the causes and the
seriousness of the alleged crisis (Loken and Gelman 2017; Ioannidis
2007; Redish, Kummerfeld, Morris, and Love 2018).



Winsberg, Huebner, and Kukla (2013) draw attention to a different kind
of supra-empirical, ethical issue raised by the contemporary situation
of multiple authorship. What they call "radically collaborative
research" involves investigators with different forms of
expertise, as in Hardwig's example, and as is now common across
many fields, collaborating to generate an experimental result. For
Winsberg, Huebner, and Kukla, the question is not merely reliability,
but accountability. Who can speak for the integrity of the research
when it has been conducted by researchers with a variety not just of
interests, but of methodological standards, most opaque one to
another? Winsberg, Huebner, and Kukla argue that a model of the social
collaboration is needed as much as a model of the data or of the
instruments. They argue further that the laissez-faire Wisdom of
Crowds model (according to which local differences in methodological
standards will cancel each other out), while perhaps adequate if the
question is one of reliability, is not adequate for addressing these
issues of accountability. They do not themselves, however, offer an
alternative model.


## 3. Science in Society



Work on the role of science in society encompasses both general models
of the public authority of science and analysis of particular research
programs that have a bearing on public life. In their early work,
Steve Fuller and Joseph Rouse were both concerned with political
dimensions of cognitive authority. Rouse, whose (1987) integrated
analytic and continental philosophy of science and technology, sought
to develop what might be called a critical pragmatism. This
perspective facilitated an analysis of the transformative impact of
science on human life and social relations. Rouse emphasized the
increased power over individual lives that developments in science
make possible. This can only be said to have increased with the
development of information technology. Fuller (1988) partially
accepted the empirical sociologists' claim that traditional
normative accounts of scientific knowledge fail to get a purchase on
actual scientific practices, but took this as a challenge to relocate
the normative concerns of philosophers. These should include the
distribution and circulation of knowledge claims. The task of social
epistemology of science, according to Fuller, should be regulation of
the production of knowledge by regulating the rhetorical,
technological, and administrative means of its communication. While
there has not been much uptake of Fuller's proposals as
articulated, Lee's work mentioned above begins to make detailed
recommendations that take into account the current structures of
funding and communication.



One key area of socially relevant interdisciplinary science is risk
assessment, which involves both research on the effects of various
substances or practices and the evaluation of those effects once
identified. The idea is to gain an understanding of both positive
effects and of negative effects and a method of evaluating these. This
involves integrating the work of specialists in the kind of substance
whose risks are under assessment (geneticists, chemists, physicists),
biomedical specialists, epidemiologists, statisticians, and so on. In
these cases, we are dealing not only with the problems of trust and
authority among specialists from different disciplines, but also with
the effects of introducing new technologies or new substances into the
world. The risks studied are generally of harm to human health or to
the environment. Interest in applying philosophical analysis to risk
assessment originated in response to debates about the development and
expansion of nuclear power-generating technologies. In addition, the
application of cost-benefit analysis and attempts to understand
decision-making under conditions of uncertainty became topics of
interest as extensions of formal modeling techniques (Giere 1991).
These discussions intersect with debates about the scope of rational
decision theory and have expanded to include other technologies as
well as applications of scientific research in agriculture and in the
myriad forms of biological engineering. Essays on the relation between
science and social values in risk research collected in the volume
edited by Deborah Mayo and Rachelle Hollander (1991) attempt to steer
a course between uncritical reliance on cost-benefit models and their
absolute rejection. Coming from a slightly different angle, the
precautionary principle represents an approach shifting the burden of
proof in regulatory decisions from demonstration of harm to
demonstration of safety of substances and practices. Carl Cranor
(2004) explores versions of the principle and defends its use in
certain decision contexts. Shrader-Frechette (2002) has advocated
models of ethically weighted cost-benefit analysis and greater public
involvement in risk assessment. In particular she (Shrader-Frechette
1994, 2002) has argued for including members of the public in
deliberations about health effects of and reasonable exposure limits
on environmental pollutants, especially radioactive materials.
Philosophers of science have also worked to make visible the ways in
which values play a role in the research assessing the effects of
techno-scientifically produced substances and practices themselves, as
distinct from the challenges of assigning values to identified risks
and benefits.



Douglas (2000) is an influential study of toxicological research on
effects of exposure to dioxins. Douglas set her analysis in the
framework of inductive risk introduced by Richard Rudner (1953) and
also explored by Carl Hempel (1965). The ampliative character of
inductive inference means that the premises can be true (and even
strongly supportive) and the conclusion false. Rudner argued that this
feature of inductive inference means that scientists ought to take the
consequences of being wrong into account when determining how strong
the evidence for a hypothesis needs to be before accepting the
hypothesis. [But see Jeffrey (1956) for a different view.] Douglas
proposes that such considerations reach deeper into the scientific
process than the acceptance of a conclusion based on the evidence to
the construction of the evidence itself. Scientists must make
decisions about levels of statistical significance, how to balance the
chance of false positives against the chance of false negatives. They
must determine protocols for deciding borderline cases in their tissue
samples. They must select among possible dose-response models.
Deciding in one way has one set of social consequences, and in another
way another, opposing, set of consequences. Douglas claims that
scientists ought to take these risks into account when making the
relevant methodological decisions. Since, even in her examples, public
health considerations point in one direction and economic
considerations point in another, in the end it is not clear just what
responsibility can reasonably be assigned to the individual
scientist.



In addition to risk assessment, philosophers have begun thinking about
a variety of research programs and methods that affect human
wellbeing. Lacey (2005), for example, delineates the contrasting
values informing industrial, conventional agriculture on the one hand
and small-scale agroecology on the other. Cartwright (2012),
elaborated in Cartwright and Hardie (2012), is primarily a critical
analysis of the reliance on randomized control trials to support
policy decisions in economic development, medicine, and education.
These fail to take account of variations in contexts of application
that will affect the outcome. Cartwright's focus on a particular
methodological approach is an extension of philosophers'
traditional engagement in areas of controversy in which philosophical
analysis might make a difference. Philip Kitcher's (1985), which
took on sociobiology, and Elliott Sober and David Sloan Wilson's
(1998), an extensive argument for group level selection, are examples
that focus on content and methodology of extensions of evolutionary
theory.



Climate change research has provoked several quite different kinds of
analysis. As a complex interdisciplinary field, its evidential
structure leaves it vulnerable to challenge. Opponents of limiting the
use of fossil fuels have exploited those vulnerabilities to sow public
doubts about the reality and/or causes of climate change (Oreskes and
Conway 2011). Parker 2006, Lloyd 2010, Parker 2010, Winsberg 2012
have, respectively, investigated strategies for reconciling apparent
inconsistencies among climate models, the differences between
model-based projections and strictly inductive projections, methods
for assessing and communicating the uncertainties inherent in climate
models. Philosophers have also considered how to interpret the
(American) public's susceptibility to the climate change
deniers. Philip Kitcher (2012) interprets it as lack of information
amid a plethora of misinformation and proposes methods for more
effective communication of reputable science to the public. Anderson
(2011), on the contrary, contends that members of the public are
perfectly able to evaluate the reliability of contradictory
assessments by following citation trails, etc., whether on the
internet or in hard copies of journals. Her view is that the
reluctance to accept the reality of climate change is a reluctance to
abandon familiar ways of life, which is what averting climate-caused
disaster requires all to do. Finally, there is an ethical and
political question once the inevitability of climate change is
accepted: how should the burdens of taking action be distributed? The
industrialized West is responsible for most of the carbon pollution up
to the end of the 20th century, but developing nations trying to
industrialize have contributed an increasing share, and will continue
to do so, in the 21st century. Who bears the burden? And if the
effects will only be felt by generations in the future, why should
present generations take actions whose harms will be felt now and
whose benefits lie in the future and will not be experienced by those
bearing the costs? Broome (2008) explores the intergenerational
issues, while Raina (2015) explores the global dimensions.



Two additional areas of ongoing scientific controversy are the
biological reality (or not) of race and the biology of gender
differences. Developments in genetics, and documented racial
differences in health, have thrown doubt on earlier anti-realist views
of race, such as those articulated by Stephen J. Gould (1981) and
Richard Lewontin (Lewontin, Rose, and Kamin 1984). Spencer (2012,
2014) argues for a sophisticated form of biological racial realism.
Gannett (2003) argues that biological populations are not independent
objects that can provide data relevant to racial realism, while Kaplan
and Winther (2013) argue that no claims about race can be read from
biological theory or data. The reality and basis of observed gender
differences were the subject of much debate in the late 20th
century(See Fausto-Sterling 1992). These issues have crystallized in
the early 21st century in debates about the brain and cognition
drawing the attention of philosophers of biology and cognitive
scientists. Rebecca Jordan-Young (2010), Cordelia Fine (2010), and
Bluhn, Jacobson and Maibom, eds. (2012) all explore, with an aim of
debunking, claims of gendered brains. 


## 3. Social, Cultural, and Feminist Studies of Science



Kuhn's critique of logical empiricism included a strong
naturalism. Scientific rationality was to be understood by studying
actual episodes in the history of science, not by formal analyses
developed from a priori concepts of knowledge and reason (Kuhn 1962,
1977). Sociologists and sociologically inclined historians of science
took this as a mandate for the examination of the full spectrum of
scientists' practices without any prior prejudice as to which
were epistemically legitimate and which not. That very distinction
came under suspicion from the new social scholars, often labeled
"social constructivists." They urged that understanding
the production of scientific knowledge required looking at all the
factors causally relevant to the acceptance of a scientific idea, not
just at those the researcher thinks should be relevant.



A wide range of approaches in social and cultural studies of science
has come under the umbrella label of "social
constructivism." Both terms in the label are understood
differently in different programs of research. While constructivists
agree in holding that those factors treated as evidential, or as
rationally justifying acceptance, should not be privileged at the
expense of other causally relevant factors, they differ in their view
of which factors are causal or worth examination. Macro-analytic
approaches, such as those associated with the so-called Strong
Programme in the Sociology of Scientific Knowledge, treat social
relations as an external, independent factor and scientific judgment
and content as a dependent outcome. Micro-analyses or laboratory
studies, on the other hand, abjure the implied separation of social
context and scientific practice and focus on the social relations
within scientific research programs and communities and on those that
bind research-productive and research-receptive communities
together.



Researchers also differ in the degree to which they treat the social
and the cognitive dimensions of inquiry as independent or interactive.
The researchers associated with the macro-analytic Strong Programme in
the Sociology of Scientific Knowledge (Barry Barnes, David Bloor,
Harry Collins, Donald MacKenzie, Andrew Pickering, Steve Shapin) were
particularly interested in the role of large scale social phenomena,
whether widely held social/political ideologies or group professional
interests, on the settlement of scientific controversies. Some
landmark studies in this genre include Andrew Pickering's (1984)
study of competing professional interests in the interpretation of
high energy particle physics experiments, and Steven Shapin and Simon
Shaffer's (1985) study of the controversy between Robert Boyle
and Thomas Hobbes about the epistemological relevance of experiments
with vacuum pumps.



The micro-sociological or laboratory studies approach features
ethnographic study of particular research groups, tracing the myriad
activities and interactions that eventuate in the production and
acceptance of a scientific fact or datum. Karin Knorr Cetina's
(1981) reports her year-long study of a plant science laboratory at UC
Berkeley. Bruno Latour and Steven Woolgar's (1986) study of
Roger Guillemin's neuroendocrinology laboratory at the Salk
Institute is another classic in this genre. These scholars argued in
subsequent work (Knorr-Cetina 1983; Latour, 1987) that their form of
study showed that philosophical analyses of rationality, of evidence,
of truth and knowledge, were irrelevant to understanding scientific
knowledge. Sharon Traweek's (1988) comparative study of the
cultures of Japanese and North American high energy physics
communities pointed to the parallels between cosmology and social
organization but abstained from making extravagant or provocative
epistemological claims. The efforts of philosophers of science to
articulate norms of scientific reasoning and judgment were, in the
view of both macro- and micro-oriented scholars, misdirected, because
actual scientists relied on quite different kinds of considerations in
the practice of science.



Until recently, apart from a few anomalous figures like Caroline
Herschel, Barbara McClintock, and Marie Curie, the sciences were a
male preserve. Feminist scholars have asked what bearing the
masculinity of the scientific profession has had on the content of
science and on conceptions of scientific knowledge and practice.
Drawing both on work by feminist scientists that exposed and critiqued
gender biased science and on theories of gender, feminist historians
and philosophers of science have offered a variety of models of
scientific knowledge and reasoning intended to accommodate the
criticism of accepted science and the concomitant proposal and
advocacy of alternatives. Evelyn Keller (1985) proposed a
psycho-dynamic model of knowledge and objectivity, arguing that a
certain psychological profile, facilitated by typical patterns of
masculine psychological development, associated knowledge and
objectivity with domination. The association of knowledge and control
continues to be a topic of concern for feminist thinkers as it is also
for environmentally concerned critics of the sciences. In this
connection, see especially Lacey's (2005) study of the
controversy concerning transgenic crops. Other feminists turned to
Marxist models of social relations and developed versions of
standpoint theory, which holds that the beliefs held by a group
reflect the social interests of that group. As a consequence, the
scientific theories accepted in a context marked by divisions of power
such as gender will reflect the interests of those in power.
Alternative theoretical perspectives can be expected from those
systematically excluded from power. (Harding 1986; Rose 1983; Haraway
1978).



Still other feminists have argued that some standard philosophical
approaches to the sciences can be used to express feminist concerns.
Nelson (1990) adopts Quine's holism and naturalism to analyze
debates in recent biology. Elizabeth Potter (2001) adapts Mary
Hesse's network theory of scientific inference to analyse
gendered aspects of 17th century physics. Helen Longino (1990)
develops a contextual empiricism to analyze research in human
evolution and in neuroendocrinology. In addition to the direct role
played by gender bias, scholars have attended to the ways shared
values in the context of reception can confer an a priori
implausibility on certain ideas. Keller (1983) argued that this was
the fate of Barbara McClintock's unorthodox proposals of genetic
transposition. Stephen Kellert (1993) made a similar suggestion
regarding the then resistance to so-called chaos theory, that is the
use of non-linear dynamics to model processes like climate change.



What the feminist and empirical sociological analyses have in common
is the view that the social organization of the scientific community
has a bearing on the knowledge produced by that community. There are
deep differences, however, in their views as to what features of that
social organization are deemed relevant and how they are expressed in
the theories and models accepted by a given community. The gender
relations focused on by feminists went unrecognized by sociologists
pursuing macro- or microsociological research programs. The feminist
scientists and scholars further differ from the scholars in empirical
social and cultural studies of science in their call for alternative
theories and approaches in the sciences. These calls imply that
philosophical concerns with truth and justification are not only
legitimate but useful tools in advancing feminist transformative goals
for the sciences. As can be seen in their varying treatments of
objectivity, however, philosophical concepts are often reworked in
order to be made applicable to the content or episodes of interest
(See Anderson 2004, Haraway 1988, Harding 1993, Keller 1985, Longino
1990, Nelson 1990, Wylie 2005)



In addition to differences in analysis of philosophical concepts like
objectivity, rationality, or truth, feminist philosophers of science
have also debated the proper role of contextual (sometimes called,
"external" or "social") values. Some feminists
argue that, given that values do play a role in scientific inquiry,
socially progressive values ought to shape not only decisions about
what to investigate but also the processes of justification.
Philosophers of science should incorporate exemplification of the
right values in their accounts of confirmation or justification.
Others are less certain about the identification of the values that
should and those that should not inform the conduct of science. These
philosophers are dubious that a consensus exists, or is even possible
in a pluralistic society, on what constitute the values that ought to
guide inquiry. In an exchange with Ronald Giere, Janet Kourany (2003a,
2003b) argues that not only science, but philosophy of science ought
to be concerned with the promotion of socially progressive values.
Giere (2003) replies that what counts as socially progressive will
vary among philosophers, and that in a democracy, it is unlikely that
a unanimous or near unanimous consensus regarding the values to inform
philosophical analysis or scientific inquiry could be achieved either
in the larger society or in the smaller social subset of philosophers
of science.


## 4. Models of the Social Character of Knowledge



Since 1980, interest in developing philosophical accounts of
scientific knowledge that incorporate the social dimensions of
scientific practice has been on the increase. Some philosophers see
attention to the social as a straightforward extension of already
developed approaches in epistemology. Others, inclined toward some
form of naturalism, have taken the work in empirical social studies of
science discussed above seriously. They have, however, diverged quite
considerably in their treatment of the social. Some understand the
social as biasing or distorting, and hence see the social as opposed
to or competing with the cognitive or epistemic. These philosophers
see the sociologists' disdain for normative philosophical
concerns as part of a general debunking of science that demands a
response and defense. Some philosophers see the social aspects of
science as incidental to deep questions about knowledge, but
informative about certain tendencies in scientific communities. Others
treat the social as instead constitutive of rationality. These
differences in conception of the role and nature of the social inform
differences in the several approaches to modeling the sociality of
inquiry and knowledge discussed below.



Contemporary philosophers pursue both formal and informal modeling
approaches in addressing the social character of knowledge. Those
pursuing formal models tend to bracket questions about rationality,
objectivity, or justification and concentrate on mathematically
investigating the effects of community structures on features of the
pursuit of knowledge and its diffusion in a community. Those pursuing
informal models are more interested in understanding the role of the
community in enhancing or constituting desired features of inquiry
such as rationality and objectivity and in thinking about the ways
knowledge is realized



*Communication and the division of cognitive labor.* Among the
first issues to be investigated using formal techniques was the
division of cognitive labor. While big science projects such as
discussed by Hardwig pose a problem of integrating disparate elements
of the solution to a question, the division of cognitive labor
concerns the appropriate or optimal distribution of efforts towards
solving a given problem. If everyone follows the same research
strategy to solve a problem or answer a question, then a solution
lying outside that strategy will not be reached. If such a solution is
better than any attainable via the shared strategy, the community
fails to attain the better solution. But how can it be rational to
adopt a research strategy other than the one deemed at the time most
likely to succeed? Philip Kitcher in his (1993) was concerned to offer
an alternative to the strong programme's proposal that
controversy and the persistence of alternative research programs were
a function of the varying social or ideological commitments of
researchers. However, he also acknowledged that if researchers
followed only the strategy judged at the time most likely to lead to
truth, they would not pursue unorthodox strategies that might lead to
new discoveries. He therefore labeled the observed fact that
researchers pursued different approaches to the same problem as the
division of cognitive labor and proposed a decision model that
attributed the pursuit of a nonorthodox (maverick) research strategy
to a rational calculation about the chances of a positive payoff. This
chance was calculated on the basis of the likelihood of the maverick
strategy being successful (or more successful than the orthodox
approach), the numbers of peers pursuing orthodox or other maverick
strategies, and the anticipated reward of success. A community can
allocate research resources in such a way as to maintain the balance
of orthodox and maverick scientists most likely to facilitate
progress. Thus, scientific progress can tolerate and indeed benefits
from a certain amount of "impure" motivation. Michael
Strevens (2003) argued instead that the pursuit of maverick research
strategies was to be expected as a consequence of the priority rule.
The priority rule refers to the practice of referring to a law or
object with the name of the first individual to articulate or perceive
and identify it. Think of Boyle's Law, Halley's comet, the
Planck constant, Avogadro's number, etc. There's no such
reward attached to pursuing a research strategy devised by another and
"merely" adding to what that individual has already
discovered. The rewards of research come from being first. And to be
first requires pursuing a novel problem or strategy. The division of
cognitive labor, understood as different researchers pursuing
different research strategies, is a simple effect of the priority
rule. Muldoon and Weisberg (2011) reject both Kitcher's and
Strevens's accounts as presupposing unrealistically uniform and
ideal agents. In reality, they observe, scientists have at best
imperfect knowledge of the entire research situation, do not know the
entirety of the research landscape, and when they do know, know
different things. They do not have sufficient information to employ
the decision methods Kitcher and Strevens attribute to them. Muldoon
and Weisberg propose agent-based modeling as a means to represent the
imperfect, non-overlapping, and partial knowledge of the agents
deciding what research problems and strategies to pursue.
Solomon's advocacy of dissensus discussed below can be
understood as rejecting the premises of the problem. From that point
of view the aim of scientific organization ought to be to promote
disagreement.



Kevin Zollman, following Bala and Goyal (1998), used network theory to
model different possible communication structures. The aim of Zollman
(2007, 2013) is to investigate what difference communication
structures make to the chances of a scientific community settling on a
correct (or incorrect) theory or hypothesis and to the speed by which
such a consensus is reached. Networks consist of nodes and edges that
connect them. The nodes can represent individuals or any group that
has uniform beliefs. The nodes can have values of believe or not
believe and consensus consists in all nodes in the network taking the
same value. Zollman investigates three possible communication
structures: the cycle, in which each node is connected only to nodes
on either side of it in the cycle; the wheel, in which there is a
central node to which all other nodes are exclusively connected; and
the complete, in which each node is connected to every other node.
Using the mathematics of network theory, Zollman proves the somewhat
counterintuitive thesis that the network with limited communication,
the cycle, has the highest probability of consensus on the correct
hypothesis, while the network with the densest communication, the
complete, has a non-negligible probability of consensus (from which
departure is not possible) on the incorrect hypothesis. Zollman (2010)
also uses this method to investigate the division of labor problem,
although he comes at it from a slightly different point of view that
do Kitcher or Strevens. Structures with sparse or limited
communication are more likely to arrive at the correct hypothesis, but
because they take longer to reach consensus, different research
approaches may persist in such communities. Under the right
circumstances, this will prevent foreclosure on the incorrect
hypothesis. Zollman implicitly blames a dense communication structure
for the premature abandonment of the bacterial hypothesis of peptic
ulcers. Diversity is a good thing as long as the evidence is not
decisive, and if the acid hypothesis, which held sway until a new
staining method showed the presence of *Helicobacter pylori*, had
been slower to diffuse into the community, the bacterial hypothesis
might have been preserved long enough to be better supported.



While Zollman presents his results as an alternative method to the
reward mechanisms discussed by Kitcher, Strevens, and Muldoon and
Weisberg, they do not include a mechanism for establishing any of the
network structures as the preferred communication system for a
scientific community. Kitcher and the others were concerned with how
agents might be motivated to pursue a theory or method whose chance of
success was either unknown or thought unlikely. Funding bodies like
governmental science foundations and private foundations provide or
can provide the relevant reward structure. Prize-giving bodies, like
the Nobel Foundation or the Kavli Foundation, as well as historical
practice, entrench the priority rule. Both of these are community
methods that can motivate the choice to pursue high risk, high reward
research. It is not clear how communities would select communication
structures, nor what kind of system would be able to enforce a
structure. Rosenstock, O'Connor, and Bruner (2017) point out in
addition that Zollman's results are very sensitive to how
parameters of the models are set. Adjust the number of nodes or the
probabilities assigned to the alternative strategies/hypotheses and
the Zollman effect disappears. The probability of consensus on the
incorrect hypothesis in the densely connected communication structure
reduces to close to zero with more nodes or greater disparity of
assigned probabilities to alternatives. 



O'Connor and other colleagues have used evolutionary game theory
to model other community phenomena such as the persistence of minority
disadvantage in scientific communities (Rubin & O'Connor
2018), scientific polarization (O'Connor & Weatherall 2017),
diversity (O'Connor & Bruner 2017), conservatism in science
(O'Connor forthcoming). While not necessarily claiming that
these game theoretic models are fully descriptive of the phenomena
they model, these theorists do claim that given certain initial
conditions, certain undesirable social situations (like the
disadvantage accruing to minority status) are to be expected rather
than being understood as perversions of scientific practice. This
would suggest that some ways of addressing those undesirable social
outcomes may not be effective and that alternative measures ought to
be sought in case of failure.



*Sociality, rationality, and objectivity.* Philosophers who treat
the social as biasing or distorting tend to focus on the
constructivists' view that there are no universal principles of
rationality or principles of evidence that can be used to identify in
any context-independent way which factors are evidential and which
not. Reconciliationists tend to argue that what is correct in the
sociologists' accounts can be accommodated in orthodox accounts
of scientific knowledge. The key is sifting the correct from the
exaggerated or misguided. Integrationists read the relevance of the
sociologists' accounts as supporting the development of new
accounts of rationality or objectivity, rather than as grounds for
rejecting the cogency of such normative ideals. 



Philosophers concerned to defend the rationality of science against
sociological misrepresentations include Larry Laudan (1984) James
Brown (1989, 1994), Alvin Goldman (1987, 1995) and Susan Haack (1996).
The details of these philosophers' approaches differ, but they
agree in holding that scientists are persuaded by what they regard as
the best evidence or argument, the evidence most indicative of the
truth by their lights, and in holding that arguments and evidence are
the appropriate focus of attention for understanding the production of
scientific knowledge. When evidential considerations have not trumped
non-evidential considerations, we have an instance of bad science.
They read the sociologists as arguing that a principled distinction
between evidential and nonevidential considerations cannot be drawn
and devote considerable effort to refuting those arguments. In their
positive proposals for accommodating the social character of science,
sociality is understood as a matter of the aggregation of individuals,
not their interactions, and public knowledge as simply the additive
outcome of many individuals making sound epistemic judgments.
Individual rationality and individual knowledge are thus the proper
focus of philosophers of science. Exhibiting principles of rationality
applicable to individual reasoning is sufficient to demonstrate the
rationality of science, at least in its ideal form.



Reconciliationists include Ronald Giere, Mary Hesse, and Philip
Kitcher. Giere (1988) models scientific judgment using decision
theory. This permits incorporating scientists' interests as one
of the parameters of the decision matrix. He also advocates a
satisficing, rather than optimizing, approach to modeling the decision
situation, thus enabling different interests interacting with the same
empirical base to support different selections as long as they are
consistent with that base. Mary Hesse (1980) employs a network model
of scientific inference that resembles W.V.O. Quine's web of
belief in that its constituents are heterogeneous in character, but
all subject to revision in relation to changes elsewhere in the
network. She understands the social factors as coherence conditions
operating in tandem with logical constraints to determine the relative
plausibility of beliefs in the network.



The most elaborate reconciliationist position is that developed in
Philip Kitcher's (1993). In addition to modeling relations of
authority and the division of cognitive labor as described above, he
offers what he terms a compromise between extreme rationalists and
sociological debunkers. The compromise model appeals to a principle of
rationality, which Kitcher calls the External Standard. It is deemed
external because it is proposed as holding independently of any
particular historical, cultural or social context. Thus, not only is
it external, but it is also universal. The principle applies to change
of belief (or shift from one practice to another, in Kitcher's
broader locution), not to belief. It treats a shift (in practice or
belief) as rational if and only "the process through which the
shift was made has a success ratio at least as high as that of any
other process used by human beings (ever) ..." (Kitcher 1993,
303). Kitcher's compromise proposes that scientific ideas
develop over time and benefit from the contributions of many
differently motivated researchers. This is the concession to the
sociologically oriented scholars. In the end, however, those theories
that are rationally accepted are those that satisfy Kitcher's
External Standard. Kitcher thus joins Goldman, Haack, and Laudan in
the view that it is possible to articulate a priori conditions of
rationality or of epistemic warrant that operate independently of, or,
perhaps one might say, orthogonally to, the social relations of
science.



A third set of models is integrationist in character. Integrationists
use the observations of sociologists of science to develop alternative
accounts of scientific rationality and objectivity. Nelson (1990)
focuses on a slightly different aspect of Quine's holism than
does Hesse. Nelson uses Quine's arguments against the
independently foundational status of observation statements as the
basis for what she calls a feminist empiricism. According to Nelson,
no principled distinction can be made between the theories,
observations, or values of a community. What counts as evidence, in
her view, is fixed by the entire complex of a community's
theories, value commitments, and observations. There is neither
knowledge nor evidence apart from such a shared complex. The community
is the primary knower on this view and individual knowledge is
dependent on the knowledge and values of the community.



Miriam Solomon's social empiricism is focused on scientific
rationality (Solomon 2001). It, too, involves denying a universal
principled distinction among the causes of belief. Solomon draws on
contemporary cognitive science literature to argue that what are
traditionally called biases are simply among the kinds of
"decision vector" that influence belief. They are not
necessarily undesirable elements from which science needs to be
protected, and can be productive of insight and rational belief.
Salience and availability (of data, of measurement technologies), also
called cold biases, are decision vectors as much as social ideologies
or other motivational factors, "hot biases." The
distinctive feature of Solomon's social empiricism is her
contrast between individual and community rationality. Her (2001)
urges the pluralistic view that a community is rational when the
theories it accepts are those that have unique empirical successes.
Individuals can persist in beliefs that are (from a panoptic
perspective) less well supported than others on this view, if the
totality of available evidence (or empirical data) is not available to
them, or when their favored theory accounts for phenomena not
accounted for other theories, even when those may have a greater
quantity of empirical successes. What matters to science, however, is
that the aggregated judgments of a community be rational. A community
is rational when the theories it accepts are those with all or with
unique empirical successes. It is collectively irrational to jettison
a theory with unique empirical successes. Thus, the community can be
rational even when its members are, as judged by traditional epistemic
standards, individually irrational. Indeed, individual irrationality
can contribute to community rationality in that individuals committed
to a theory that accounts for their data keep that data in the range
of phenomena any theory accepted by the entire community must
eventually explain. In addition to empirical success, Solomon proposes
an additional normative criterion. In order to secure appropriate
distribution of scientific effort, biases must be appropriately
distributed in the community. Solomon proposes a scheme for
ascertaining when a distribution is normatively appropriate. Thus, for
Solomon, a scientific community is rational when biases are
appropriately distributed and it accepts only a theory with all or
theories with unique empirical successes as the normative
epistemological condition. Rationality accrues only to a community,
and not to the individuals constituting the community. As in
Zollman's network models, consensus just is all members of the
community assigning the same value (T/F) to a hypothesis or
theory.



Finally, in Longino's critical contextual empiricism, the
cognitive processes that eventuate in scientific knowledge are
themselves social (Longino 1990, 2002). Longino's starting point
is a version of the underdetermination argument: the semantic gap
between statements describing data and statements expressing
hypotheses or theories to be confirmed or disconfirmed by that data.
This gap, created by the difference in descriptive terms used in the
description of data and in the expression of hypotheses, means that
evidential relations cannot be formally specified and that data cannot
support one theory or hypothesis to the exclusion of all alternatives.
Instead, such relations are mediated by background assumptions.
Eventually, in the chain of justification, one reaches assumptions for
which no evidence is available. If these are the context in which
evidential relations are constituted, questions arise concerning how
the acceptance of such assumptions can be legitimated. According to
Longino, the only check against the arbitrary dominance of subjective
(metaphysical, political, aesthetic) preference in such cases is
critical interaction among the members of the scientific community or
among members of different communities. There is no higher authority
or transcendent aperspectival position from which it is possible to
adjudicate among foundational assumptions. Longino takes the
underdetermination argument to express in logical terms the point made
by the sociologically oriented researchers: the individuals
participating in the production of scientific knowledge are
historically, geographically, and socially situated and their
observations and reasoning reflect their situations. This fact does
not undermine the normative enterprise of philosophy, but requires its
expansion to include within its scope the social interactions within
and between scientific communities. What counts as knowledge is
determined by such interactions.



Longino claims that scientific communities do institutionalize some
critical practices (for example, peer review), but argues that such
practices and institutions must satisfy conditions of effectiveness in
order to qualify as objective. She argues, therefore, for the
expansion of scientific norms such as accuracy and consistency to
include norms that apply to communities. These are (1) the provision
of venues in which critical interaction can take place, (2) the uptake
of critical intervention as demonstrated in change of belief
distribution in the community over time in a way that is sensitive to
the critical discourse taking place within that community, (3) public
accessibility of the standards that regulate discourse, and (4)
tempered equality of intellectual authority. By this latter condition,
perhaps the most controversial of her proposed norms, Longino means
that any perspective has a prima facie capacity to contribute to the
critical interactions of a community, though equal standing can be
lost owing to failure to engage or to respond to criticism. In her
2002, Longino argues that the cognitive processes of science, such as
observation and reasoning, are themselves social processes. Thus the
interactions subject to community norms extend not only to discussion
of assumptions in finished research, but to the constructive processes
of research as well.



Solomon and Longino differ on where they locate normativity and on the
role and effectiveness of deliberative processes in actual scientific
inquiry. Solomon attends to the patterns of acceptance and to the
distribution of decision vectors, regardless of the interactions among
community members, while Longino attends to deliberative processes and
interactions. They may also differ in their views of what constitutes
scientific success.



One set of issues that has yet to give rise to extended philosophical
reflection is the question how civilizational differences are
expressed in scientific work (See Bala 2008). Here, too, there is a
micro- and a macro- version. At the micro level, one might ask how the
interactional culture of individual laboratories or theoretical
subcommunities is or is not expressed in the outcome of their
research. At the macro level one might be asking how large scale
cultural features are reflected in the content and practice of science
in a given cultural formation. For example, Joseph Needham argued that
features of the culture of ancient China directed their technical and
intellectual ingenuity into channels that foreclosed the development
of anything like the science that developed in Western Europe in the
14th through the 17th centuries. Other cultures developed some aspects
of what we now think of as a cosmopolitan or global scientific culture
(for example, the mathematics and astronomy of 10th through 14th
century Islamic and South Asian scholars) independently of the early
modern physics developed in Western and Central Europe. The papers in
Habib and Raina (2001) address aspects of these questions with respect
to the history of science in India.



*Unity, Plurality and the Aims of Inquiry.* The variety of views
on the degree of sociality assignable to the epistemological concepts
of science lead to different views concerning the ultimate character
of the outcome of inquiry. This difference can be summarized as the
difference between monism and pluralism. Monism, as characterized in
Kellert, Longino, and Waters (2006), holds that the goal of inquiry is
and should be a unified, comprehensive, and complete account of
phenomena (whether all phenomena, or the phenomena specific to a
particular domain of inquiry). If this is so, then the norms of
assessment should be informed by this goal and there should be one
standard by which theories, models, and hypotheses in the sciences are
assessed. Deviation from an accepted theoretical framework is
problematic and requires explanation, such as the explanations offered
for the division of cognitive labor. Monism, with its commitment to
ultimate unity, requires ways to reconcile competing theories or to
adjudicate controversy so as to eliminate competition in favor of the
one true or best theory. Pluralism, on the other hand, holds that the
observed plurality of approaches within a science is not necessarily a
flaw but rather reflects the complexity of the phenomena under
investigation in interaction with the limitations of human cognitive
capacities and the variety of human cognitive as well as pragmatic
interests in representations of those phenomena.



Among pluralists, a diversity of views is to be found. Suppes (1978)
emphasized the mutual untranslatability of the descriptive terms
developed in the course of scientific specialization. Such
incommensurability will resist evaluation by a common measure.
Cartwright's (1999) invocation of a dappled world emphasizes the
complexity and diversity of the natural (and social) world. Scientific
theories and models are representations of varying degrees of
abstraction that manage to apply at best partially to whatever
phenomena they purport to represent. To the extent they are taken to
represent actual process in the real world, they must be hedged by
ceteris paribus clauses. Scientific laws and models attach to patches
of the world, but not to a seamlessly law-governed whole.
Mitchell's (2002, 2009) integrative pluralism is a rejection of
the goal of unification by either reduction to a single (fundamental)
level of explanation or abstraction to a single theoretical
representation, in favor of a more pragmatically inflected set of
explanatory strategies. The success for any particular investigation
is answerable to the goals of the investigation, but there may be
multiple compatible accounts reflecting both the contingency and
partiality of the laws/generalizations that can figure in explanations
and the different goals one may bring to investigation of the same
phenomenon. The explanations sought in any particular explanatory
situation will draw on these multiple accounts as appropriate for the
level of representation adequate to achieve its pragmatic ends.
Mitchell's defense of integrative pluralism rests on both the
partiality of representation and the complexity of the phenomena to be
explained.



Kellert, Longino, and Waters advance a pluralism that sees
multiplicity not only among but within levels of analysis. Furthermore
they see no reason to require that the multiple accounts be
compatible. The multiplicity of noncongruent empirically adequate
accounts helps us appreciate the complexity of a phenomenon without
being in a position to generate a single account of that complexity.
They do not hold that all phenomena will support ineliminable
pluralism, but that there are some phenomena that will require
mutually irreducible or incompatible models. Which these are is
determined by examining the phenomena, the models, and the match
between phenomena and models. Like Mitchell, Kellert, Longino, and
Waters hold that pragmatic considerations (broadly understood) will
govern the choice of model to be used in particular circumstances.
Both forms of pluralism (compatibilist and noncompatibilist) abandon
the notion that there is a set of natural kinds whose causal
interactions are the basis for fundamental explanations of natural
processes. The noncompatibilist is open to multiple classification
schemes answerable to different pragmatic interests in classifying. To
this extent the noncompatibilist pluralist embraces a view close to
the promiscuous realism articulated by John Dupre (1993). The
compatibilist, or integrative pluralist, on the other hand, must hold
that there is a way that different classification schemes can be
reconciled to support the envisioned integration of explanatory
models.



Pluralism receives support from several additional approaches. Giere
(2006) uses the phenomenon of color vision to support a position he
calls perspectival realism. Like the colors of objects, scientific
representations are the result of interactions between human cognitive
faculties and the world. Other species have different visual equipment
and perceive the world differently. Our human cognitive faculties,
then, constitute perspectives. We could have been built differently
and hence perceived the world differently. Perspectival realism leads
to pluralism, because perspectives are partial. While van
Fraassen's (2008) does not take a position on pluralism vs.
monism (and as an empiricist and antirealist van Fraassen would not
have to), its emphasis on the partiality and perspective dependence of
measurement provides a complementary point of entry to such diversity.
Solomon (2006) urges a yet more welcoming attitude towards
multiplicity. In her view, dissensus is a necessary component of
well-functioning scientific communities and consensus can be
epistemologically pernicious. In an extension of the arguments in
Solomon (2001) she argues that different models and theoretical
representations will be associated with particular insights or
specific data that are likely to be lost if the aim is to integrate or
otherwise combine the models to achieve a consensus understanding. The
activity of integrating two or more models is different from the
process of one model from a set of alternatives coming eventually to
have all the empirical successes distributed among the other models.
In her examination of consensus conferences called by the United
States National Institutes of Health (Solomon 2011), Solomon finds
that such conferences do not resolve existing dissent in the
scientific community. Instead, they tend to take place after a
consensus has emerged in the research community and are directed more
to the communication of such consensus to outside communities (such as
clinicians, insurers, health policy experts, and the public) than to
the assessment of evidence that might warrant consensus.



Researchers committed to a monist or unified science will see
plurality as a problem to be overcome, while researchers already
committed to a deeply social view of science will see plurality as a
resource of communities rather than a problem. The diversity and
partiality that characterizes both a local and the global scientific
community characterize the products of those communities as well as
the producers. Universalism and unification require the elimination of
epistemologically relevant diversity, while a pluralist stance
promotes it and the deeply social conception of knowledge that
follows. 



*Sociality and the structure of scientific knowledge.* Attention
to the social dimensions of scientific knowledge and the consequent
potential for plurality has prompted philosophers to rethink the
structure of what is known. Many philosophers (including Giere,
Kitcher, and Longino) who advocate forms of pluralism invoke the
metaphor of maps to explain how scientific representations can be both
partial and adequate. Maps only represent those features of the
territory mapped that are relevant for the purpose for which the map
is drawn. Some maps may represent the physical area bounded by state
boundaries, others may represent the population size, or the relative
abundance/poverty of natural resources. Winther (forthcoming) explores
the variety of kinds of maps used in science and philosophical use of
the map metaphor. But the map metaphor is only one of several ways to
rethink the structure of scientific knowledge.



Other philosophers draw more heavily on cognitive science. Giere
(2002) takes a naturalist approach to modeling, not so much the
distribution of cognitive labor, but the distribution of cognition.
This approach takes a system or interactive community as the locus of
cognition, rather than the individual agent. Nersessian (2006) extends
distributed cognition to model-based reasoning in the sciences. Models
are artifacts that focus the cognitive activity of multiple
individuals in particular settings. Knowledge is distributed across
the minds interacting about the artifacts in that setting. Paul
Thagard draws on the increasingly interdisciplinary (and hence social)
nature of cognitive science itself to argue that not only does
cognitive science (or certain lines of analysis in cognitive science)
support a conception of cognition as distributed among interacting
agents, but that this conception can be turned back upon cognitive
science itself. (Thagard 2012). Finally Alexander Bird (2010) reflects
on the sense of knowledge required for attributions such as:
"the biomedical community now knows that peptic ulcers are often
caused by the bacterium *Helicobacter pylori*." Or
"There was an explosive growth in scientific knowledge in the
twentieth century." Bird faults other social epistemologists for
still making such collective knowledge supervenient on the states of
individuals. Instead, he argues, we should understand social knowing
as a functional analogue of individual knowing. Both are dependent on
the existence and proper functioning of the relevant structures:
reasoning and perception for individuals; libraries and journals and
other social structures, for collectivities. Scientific knowledge is
an emergent effect of collective epistemic interactions, concretized
in the texts that have been designated as vehicles for the
preservation and communication of that knowledge


## 5. Social Direction of Science



Modern science has been regarded as both a model of democratic
self-governance and an activity requiring and facilitating democratic
practices in its supporting social context (Popper 1950, Bronowski
1956). In this perspective, science is seen as embedded in and
dependent on its supporting social context, but insulated in its
practices from the influence of that context. As the reach of science
and science-based technologies has extended further and further into
the economy and daily life of industrialized societies, new attention
is paid to the governance of science. Regardless of one's views
about the social character of knowledge, there are further questions
concerning what research to pursue, what social resources to devote to
it, who should make such decisions, and how they should be made.



Philip Kitcher (2001) has opened these questions to philosophical
scrutiny. While Kitcher largely endorses the epistemological views of
his (1993), in the later work he argues that there is no absolute
standard of the significance (practical or epistemic) of research
projects, nor any standard of the good apart from subjective
preferences. The only non-arbitrary way to defend judgments concerning
research agendas in the absence of absolute standards is through
democratic means of establishing collective preferences. Kitcher,
thus, attempts to spell out procedures by which decisions concerning
what research directions to pursue can be made in a democratic manner.
The result, which he calls well-ordered science, is a system in which
the decisions actually made track the decisions that would be a made
by a suitably constituted representative body collectively
deliberating with the assistance of relevant information (concerning,
e.g., cost and feasibility) supplied by experts.



Kitcher's "well-ordered science" has attracted
attention from other philosophers, from scientists, and from scholars
of public policy. Winning praise as a first step, it has also elicited
a variety of criticisms and further questions. The criticisms of his
proposal range from worries about the excessive idealism of the
conception to worries that it will enshrine the preferences of a much
smaller group than those who will be affected by research decisions.
Kitcher's proposal at best works for a system in which all or
most scientific research is publicly funded. But the proportion of
private, corporate, funding of science compared to that of public
funding has been increasing, thus calling into question the
effectiveness of a model that presupposes largely public control
(Mirowski and Sent 2002, Krimsky 2003). Kitcher's model, it
should be noted, still effects a significant separation between the
actual conduct of research and decisions concerning the direction of
research and scholars who see a more intimate relation between social
processes and values in the context and those in the conduct of
research will be dissatisfied with it. Kitcher himself (Kitcher 2011)
seems to relax the separation somewhat.



The counterfactual character of the proposal raises questions about
the extent to which well-ordered science really is democratic. If the
actual decisions do not need to be the result of democratic procedures
but only to be the same as those that would result from such
procedures, how do we know which decisions those are without actually
going through the deliberative exercise? Even if the process is
actually carried out, there are places, e.g. in choice of experts
whose advice is sought, which permit individual preferences to subvert
or bias the preferences of the whole (Roth 2003). Furthermore, given
that the effects of scientific research are potentially global, while
democratic decisions are at best national, national decisions will
have an effect well beyond the population represented by the decision
makers. Sheila Jasanoff has also commented that even in contemporary
industrialized democracies there are quite different science
governance regimes. There is not one model of democratic decision
making, but many, and the differences translate into quite different
policies (Jasanoff 2005).



In his (2011) Kitcher abandons the counterfactual approach as he
brings the ideal of well-orderedness into contact with actual debates
in and about contemporary science. His concern here is the variety of
ways in which scientific authority has been eroded by what he terms
"chimeric epistemologies." It's not enough to say
that the scientific community has concluded that, say, the MMR vaccine
is safe, or that the climate is changing in a way that requires a
change in human activities. In a democratic society, there are many
other voices claiming authority, whether on presumed evidential
grounds or as part of campaigns to manipulate public opinion. Kitcher
suggests mechanisms whereby small groups trusted by their communities
might develop the understanding of complicated technical issues
through tutoring by members of the relevant research communities and
then carry this understanding back to the public. He also endorses
James Fishkin's (2009) experiments in deliberative polling as a
means to bring members of the public committed to different sides of a
technical issue together with the scientific exponents of the issue
and in a series of exchanges that cover the evidence, the different
kinds of import different lines of reasoning possess, and the other
elements of a reasoned discussion, bring the group to a consensus on
the correct view. The pluralist and pragmatically inclined
philosophers discussed in the previous section might worry that there
is not a single correct view towards which such an encounter ought to
converge, but that a broader discussion that incorporates deliberation
about aims and values might produce sufficient (temporary) convergence
to ground action or policy.


## 6. Conclusion



Philosophical study of the social dimensions of scientific knowledge
has been intensifying in the decades since 1970. Social controversies
about the sciences and science based technologies as well as
developments in philosophical naturalism and social epistemology
combine to drive thinking in this area forward. Scholars in a number
of cognate disciplines continue to investigate the myriad social
relations within scientific communities and between them and their
social, economic, and institutional contexts.



While this area first came to prominence in the so-called science wars
of the 1980s, attending to social dimensions of science has brought a
number of topics to philosophical attention. The phenomenon of Big
Science has encouraged philosophers to consider the epistemological
significance of such phenomena as trust and cognitive interdependence
and the division of cognitive labor. The increased economic and social
dependence on science-based technologies has prompted attention to
questions of inductive risk and the role of values in assessing
hypotheses with social consequences. The controversies over health
risks of certain vaccines, over the measurement of environmental
pollution, and over the causes of climate change have expanded
philosophy of science from its more accustomed areas of logical and
epistemological analysis to incorporate concerns about the
communication and uptake of scientific knowledge and the ethical
dimensions of superficially factual debates.



Partly in response to the work of scholars in the social studies of
science, partly in response to the changing role of scientific inquiry
through the 20th and into the 21st centuries, philosophers have sought
ways to either accommodate the (tenable) results of the sociologists
and cultural historians or to modify traditional epistemological
concepts used in the analysis of scientific knowledge. These
investigations in turn lead to new thinking about the structure and
location of the content of knowledge. While debates within philosophy
of science between and among adherents to one or another of the models
of the sociality of knowledge will continue, an important future step
will be a fuller encounter between individual-based social
epistemology with its focus on testimony and disagreement as
transactions among individuals and the more fully social
epistemologies that take social relations or interaction as partially
constitutive of empirical knowledge.