## 1. A First Look: Duhem, Quine, and the Problems of Underdetermination



The scope of the epistemic challenge arising from underdetermination
is not limited only to scientific contexts, as is perhaps most readily
seen in classical skeptical attacks on our knowledge more generally.
Rene Descartes ([1640] 1996) famously sought to doubt any and
all of his beliefs which could possibly be doubted by supposing that
there might be an all-powerful Evil Demon who sought to deceive him.
Descartes' challenge appeals to a form of underdetermination: he
notes that all our sensory experiences would be just the same if they
were caused by this Evil Demon rather than an external world of rocks
and trees. Likewise, Nelson Goodman's (1955) "New Riddle
of Induction" turns on the idea that the evidence we now have
could equally well be taken to support inductive generalizations quite
different from those we usually take them to support, with radically
different consequences for the course of future
 events.[1]
 Nonetheless, underdetermination has been thought to arise in
scientific contexts in a variety of distinctive and important ways
that do not simply recreate such radically skeptical
possibilities.



The traditional locus classicus for underdetermination in science is
the work of Pierre Duhem, a French physicist as well as historian and
philosopher of science who lived at the turn of the 20th
Century. In *The Aim and Structure of Physical Theory*, Duhem
formulated various problems of scientific underdetermination in an
especially perspicuous and compelling way, although he himself argued
that these problems posed serious challenges only to our efforts to
confirm theories in physics. In the middle of the 20th
Century, W. V. O. Quine suggested that such challenges applied not
only to the confirmation of all types of scientific theories, but to
all knowledge claims whatsoever. His incorporation and further
development of these problems as part of a general account of human
knowledge was one of the most significant developments of
20th Century epistemology. But neither Duhem nor Quine was
careful to systematically distinguish a number of fundamentally
distinct lines of thinking about underdetermination found in their
work. Perhaps the most important division is between what we might
call holist and contrastive forms of underdetermination. Holist
underdetermination (Section 2 below) arises whenever our inability to
test hypotheses in isolation leaves us underdetermined in our
*response* to a failed prediction or some other piece of
disconfirming evidence. That is, because hypotheses have empirical
implications or consequences only when *conjoined* with other
hypotheses and/or background beliefs about the world, a failed
prediction or falsified empirical consequence typically leaves open to
us the possibility of blaming and abandoning one of these background
beliefs and/or 'auxiliary' hypotheses rather than the
hypothesis we set out to test in the first place. But contrastive
underdetermination (Section 3 below) involves the quite different
possibility that for any body of evidence confirming a theory, there
might well be *other theories* that are also well confirmed by
that very same body of evidence. Moreover, claims of
underdetermination of either of these two fundamental varieties can
vary in strength and character in any number of ways: one might, for
example, suggest that the choice between two theories or two ways of
revising our beliefs is *transiently* underdetermined simply by
the evidence we happen to have *at present*, or instead
*permanently* underdetermined by *all possible*
evidence. Indeed, the variety of forms of underdetermination that
confront scientific inquiry, and the causes and consequences claimed
for these different varieties, are sufficiently heterogeneous that
attempts to address "the" problem of underdetermination
for scientific theories have often engendered considerable confusion
and argumentation at
 cross-purposes.[2]



Moreover, such differences in the character and strength of various
claims of underdetermination turn out to be crucial for resolving the
significance of the issue. For example, in some recently influential
discussions of science it has become commonplace for scholars in a
wide variety of academic disciplines to make casual appeal to claims
of underdetermination (especially of the holist variety) to support
the idea that *something* besides evidence must step in to do
the further work of determining beliefs and/or changes of belief in
scientific contexts. Perhaps most prominent among these are adherents
of the sociology of scientific knowledge (SSK) movement and some
feminist science critics who have argued that it is typically the
sociopolitical interests and/or pursuit of power and influence by
scientists themselves which play a crucial and even decisive role in
determining which beliefs are actually abandoned or retained in
response to conflicting evidence. As we will see in Section 2.2,
however, Larry Laudan has argued that such claims depend upon simple
equivocation between comparatively weak or trivial forms of
underdetermination and the far stronger varieties from which they draw
radical conclusions about the limited reach of evidence and
rationality in science. In the sections that follow we will seek to
clearly characterize and distinguish the various forms of both holist
and contrastive underdetermination that have been suggested to arise
in scientific contexts (noting some important connections between them
along the way), assess the strength and significance of the
heterogeneous argumentative considerations offered in support of and
against them, and consider just which forms of underdetermination pose
genuinely consequential challenges for scientific inquiry.


## 2. Holist Underdetermination and Challenges to Scientific Rationality


### 2.1 Holist Underdetermination: The Very Idea



Duhem's original case for holist underdetermination is, perhaps
unsurprisingly, intimately bound up with his arguments for
confirmational holism: the claim that theories or hypotheses can only
be subjected to empirical testing in groups or collections, never in
isolation. The idea here is that a single scientific hypothesis does
not by itself carry any implications about what we should expect to
observe in nature; rather, we can derive empirical consequences from
an hypothesis only when it is conjoined with many other beliefs and
hypotheses, including background assumptions about the world, beliefs
about how measuring instruments operate, further hypotheses about the
interactions between objects in the original hypothesis' field
of study and the surrounding environment, etc. For this reason, Duhem
argues, when an empirical prediction is falsified, we do not know
whether the fault lies with the hypothesis we originally sought to
test or with one of the many other beliefs and hypotheses that were
also needed and used to generate the failed prediction:



> 
> A physicist decides to demonstrate the inaccuracy of a proposition; in
> order to deduce from this proposition the prediction of a phenomenon
> and institute the experiment which is to show whether this phenomenon
> is or is not produced, in order to interpret the results of this
> experiment and establish that the predicted phenomenon is not
> produced, he does not confine himself to making use of the proposition
> in question; he makes use also of a whole group of theories accepted
> by him as beyond dispute. The prediction of the phenomenon, whose
> nonproduction is to cut off debate, does not derive from the
> proposition challenged if taken by itself, but from the proposition at
> issue joined to that whole group of theories; if the predicted
> phenomenon is not produced, the only thing the experiment teaches us
> is that among the propositions used to predict the phenomenon and to
> establish whether it would be produced, there is at least one error;
> but where this error lies is just what it does not tell us. ([1914]
> 1954, 185)
> 



Duhem supports this claim with examples from physical theory,
including one designed to illustrate a celebrated further consequence
he draws from it. Holist underdetermination ensures, Duhem argues,
that there cannot be any such thing as a "crucial
experiment" (experimentum crucis): a single experiment whose
outcome is predicted differently by two competing theories and which
therefore serves to definitively confirm one and refute the other. For
example, in a famous scientific episode intended to resolve the
ongoing heated battle between partisans of the theory that light
consists of a stream of particles moving at extremely high speed (the
particle or "emission" theory of light) and defenders of
the view that light consists instead of waves propagated through a
mechanical medium (the wave theory), the physicist Foucault designed
an apparatus to test the two theories' competing claims about
the speed of transmission of light in different media: the particle
theory implied that light would travel faster in water than in air,
while the wave theory implied that the reverse was true. Although the
outcome of the experiment was taken to show that light travels faster
in air than in
 water,[3]
 Duhem argues that this is far from a refutation of the hypothesis of
emission:



> 
> in fact, what the experiment declares stained with error is the whole
> group of propositions accepted by Newton, and after him by Laplace and
> Biot, that is, the whole theory from which we deduce the relation
> between the index of refraction and the velocity of light in various
> media. But in condemning this system as a whole by declaring it
> stained with error, the experiment does not tell us where the error
> lies. Is it in the fundamental hypothesis that light consists in
> projectiles thrown out with great speed by luminous bodies? Is it in
> some other assumption concerning the actions experienced by light
> corpuscles due to the media in which they move? We know nothing about
> that. It would be rash to believe, as Arago seems to have thought,
> that Foucault's experiment condemns once and for all the very
> hypothesis of emission, i.e., the assimilation of a ray of light to a
> swarm of projectiles. If physicists had attached some value to this
> task, they would undoubtedly have succeeded in founding on this
> assumption a system of optics that would agree with Foucault's
> experiment. ([1914] 1954, p. 187)
> 



From this and similar examples, Duhem drew the quite general
conclusion that our response to the experimental or observational
falsification of a theory is always underdetermined in this way. When
the world does not live up to our theory-grounded expectations, we
must give up *something*, but because no hypothesis is ever
tested in isolation, no experiment ever tells us precisely which
belief it is that we must revise or give up as mistaken:



> 
> In sum, the physicist can never subject an isolated hypothesis to
> experimental test, but only a whole group of hypotheses; when the
> experiment is in disagreement with his predictions, what he learns is
> that at least one of the hypotheses constituting this group is
> unacceptable and ought to be modified; but the experiment does not
> designate which one should be changed. ([1914] 1954, 187)
> 



The predicament Duhem here identifies is no mere rainy day puzzle for
philosophers of science, but a methodological challenge that
consistently arises in the course of scientific practice itself. It is
simply not true that for practical purposes and in concrete contexts
there is always just a single revision of our beliefs in response to
disconfirming evidence that is obviously correct, most promising, or
even most sensible to pursue. To cite a classic example, when
Newton's celestial mechanics failed to correctly predict the
orbit of Uranus, scientists at the time did not simply abandon the
theory but protected it from refutation by instead challenging the
background assumption that the solar system contained only seven
planets. This strategy bore fruit, notwithstanding the falsity of
Newton's theory: by calculating the location of a hypothetical
eighth planet influencing the orbit of Uranus, the astronomers Adams
and Leverrier were eventually led to discover Neptune in 1846. But the
very same strategy failed when used to try to explain the advance of
the perihelion in Mercury's orbit by postulating the existence
of "Vulcan", an additional planet located between Mercury
and the sun, and this phenomenon would resist satisfactory explanation
until the arrival of Einstein's theory of general relativity. So
it seems that Duhem was right to suggest not only that hypotheses must
be tested as a group or a collection, but also that it is by no means
a foregone conclusion which member of such a collection should be
abandoned or revised in response to a failed empirical test or false
implication. Indeed, this very example illustrates why Duhem's
own rather hopeful appeal to the 'good sense' of
scientists themselves in deciding when a given hypothesis ought to be
abandoned promises very little if any relief from the general
predicament of holist underdetermination.



As noted above, Duhem thought that the sort of underdetermination he
had described presented a challenge only for theoretical physics, but
subsequent thinking in the philosophy of science has tended to the
opinion that the predicament Duhem described applies to theoretical
testing in all fields of scientific inquiry. We cannot, for example,
test an hypothesis about the phenotypic effects of a particular gene
without presupposing a host of further beliefs about what genes are,
how they work, how we can identify them, what other genes are doing,
and so on. In the middle of the 20th Century, W. V. O.
Quine would incorporate confirmational holism and its associated
concerns about underdetermination into an extraordinarily influential
account of knowledge in general. As part of his famous (1951) critique
of the widely accepted distinction between truths that are analytic
(true by definition, or as a matter of logic or language alone) and
those that are synthetic (true in virtue of some contingent fact about
the way the world is), Quine argued that *all* of the beliefs
we hold at any given time are linked in an interconnected web, which
encounters our sensory experience only at its periphery:



> 
> The totality of our so-called knowledge or beliefs, from the most
> casual matters of geography and history to the profoundest laws of
> atomic physics or even of pure mathematics and logic, is a man-made
> fabric which impinges on experience only along the edges. Or, to
> change the figure, total science is like a field of force whose
> boundary conditions are experience. A conflict with experience at the
> periphery occasions readjustments in the interior of the field. But
> the total field is so underdetermined by its boundary conditions,
> experience, that there is much latitude of choice as to what
> statements to reevaluate in the light of any single contrary
> experience. No particular experiences are linked with any particular
> statements in the interior of the field, except indirectly through
> considerations of equilibrium affecting the field as a whole. (1951,
> 42-3)
> 



One consequence of this general picture of human knowledge is that all
of our beliefs are tested against experience only as a corporate
body--or as Quine sometimes puts it, "The unit of empirical
significance is the whole of science" (1951, p.
 42).[4]
 A mismatch between what the web as a whole leads us to expect and the
sensory experiences we actually receive will occasion *some*
revision in our beliefs, but which revision we should make to bring
the web as a whole back into conformity with our experiences is
radically underdetermined by those experiences themselves. To use
Quine's example, if we find our belief that there are brick
houses on Elm Street to be in conflict with our immediate sense
experience, we might revise our beliefs about the houses on Elm
Street, but we might equally well modify instead our beliefs about the
appearance of brick, our present location, or innumerable other
beliefs constituting the interconnected web. In a pinch, we might even
decide that our present sensory experiences are simply hallucinations!
Quine's point was not that any of these are particularly likely
or reasonable responses to recalcitrant experiences (indeed, an
important part of his account is the explanation of why they are not),
but instead that they would serve equally well to bring the web of
belief as a whole in line with our experience. And if the belief that
there are brick houses on Elm Street were sufficiently important to
us, Quine insisted, it would be possible for us to preserve it
"come what may" (in the way of empirical evidence), by
making sufficiently radical adjustments elsewhere in the web of
belief. It is in principle open to us, Quine argued, to revise even
beliefs about logic, mathematics, or the meanings of our terms in
response to recalcitrant experience; it might seem a tempting solution
to certain persistent difficulties in quantum mechanics, for example,
to reject classical logic's law of the excluded middle (allowing
physical particles to both have and not have some determinate
classical physical property like position or momentum at a given
time). The only test of a belief, Quine argued, is whether it fits
into a web of connected beliefs that accords well with our experience
*on the whole*. And because this leaves any and all beliefs in
that web at least potentially subject to revision on the basis of our
ongoing sense experience or empirical evidence, he insisted, there
simply are no beliefs that are analytic in the originally supposed
sense of immune to revision in light of experience, or true no matter
what the world is like.



Quine recognized, of course, that many of the logically possible ways
of revising our beliefs in response to recalcitrant experiences that
remain open to us nonetheless strike us as ad hoc, perfectly
ridiculous, or worse. He argues (1955) that our actual revisions of
the web of belief seek to maximize the theoretical
"virtues" of simplicity, familiarity, scope, and
fecundity, along with conformity to experience, and elsewhere suggests
that we typically seek to resolve conflicts between the web of our
beliefs and our sensory experiences in accordance with a principle of
"conservatism", that is, by making the smallest possible
number of changes to the least central beliefs we can that will
suffice to reconcile the web with experience. That is, Quine
recognized that when we encounter recalcitrant experience we are not
usually at a loss to decide which of our beliefs to revise in response
to it, but he claimed that this is simply because we are strongly
disposed as a matter of fundamental psychology to prefer whatever
revision requires the most minimal mutilation of the existing web of
beliefs and/or maximizes virtues that he explicitly recognizes as
pragmatic in character. Indeed, it would seem that on Quine's
view the very notion of a belief being more central or peripheral or
in lesser or greater "proximity" to sense experience
should be cashed out simply as a measure of our willingness to revise
it in response to recalcitrant experience. That is, it would seem that
what it *means* for one belief to be located
"closer" to the sensory periphery of the web than another
is simply that we are more likely to revise the first than the second
if doing so would enable us to bring the web as a whole into
conformity with otherwise recalcitrant sense experience. Thus, Quine
saw the traditional distinction between analytic and synthetic beliefs
as simply registering the endpoints of a psychological continuum
ordering our beliefs according to the ease and likelihood with which
we are prepared to revise them in order to reconcile the web as a
whole with our sense experience as a whole.


### 2.2 Challenging the Rationality of Science



It is perhaps unsurprising that such holist underdetermination has
been taken to pose a threat to the fundamental rationality of the
scientific enterprise. The claim that the empirical evidence alone
underdetermines our response to failed predictions or recalcitrant
experience might even seem to *invite* the suggestion that what
systematically steps into the breach to do the further work of
singling out just one or a few candidate responses to disconfirming
evidence is something irrational or at least arational in character.
Imre Lakatos and Paul Feyerabend each suggested that because of
underdetermination, the difference between empirically successful and
unsuccessful theories or research programs is largely a function of
the differences in talent, creativity, resolve, and resources of those
who advocate them. And at least since the influential work of Thomas
Kuhn, one important line of thinking about science has held that it is
ultimately the social and political interests (in a suitably broad
sense) of scientists themselves which serve to determine their
responses to disconfirming evidence and therefore the further
empirical, methodological, and other commitments of any given
scientist or scientific community. Mary Hesse suggests that Quinean
underdetermination showed why certain "non-logical" and
"extra-empirical" considerations must play a role in
theory choice, and claims that "it is only a short step from
this philosophy of science to the suggestion that adoption of such
criteria, that can be seen to be different for different groups and at
different periods, should be explicable by social rather than logical
factors" (1980, 33). Perhaps the most prominent modern day
defenders of this line of thinking are those scholars in the sociology
of scientific knowledge (SSK) movement and in feminist science studies
who argue that it is typically the career interests, political
affiliations, intellectual allegiances, gender biases, and/or pursuit
of power and influence by scientists themselves which play a crucial
or even decisive role in determining precisely which beliefs are
abandoned or retained when faced with conflicting evidence (classic
works in SSK include Bloor 1991, Collins 1992, and Shapin and Schaffer
1985; in feminist science studies, see Longino, 1990, 2002, and for a
recent review, Nelson 2022). The shared argumentative schema here is
one on which holist underdetermination ensures that the evidence alone
cannot do the work of picking out a unique response to failed
predictions or recalcitrant experience, thus something else must step
in to do the job, and sociologists of scientific knowledge, feminist
critics of science, and other interest-driven theorists of science
each have their favored suggestions close to hand. (For useful further
discussion, see Okasha 2000. Note that historians of science have also
appealed to underdetermination in presenting "counterfactual
histories" exploring the ways in which important historical
developments in science might have turned out quite differently than
they actually did; see, for example, Radick 2023.) 



In response to this line of argument, Larry Laudan (1990) argues that
the significance of such underdetermination has been greatly
exaggerated. Underdetermination actually comes in a wide variety of
strengths, he insists, depending on precisely what is being asserted
about the character, the availability, and (most importantly) the
*rational defensibility* of the various competing hypotheses or
ways of revising our beliefs that the evidence supposedly leaves us
free to accept. Laudan usefully distinguishes a number of different
dimensions along which claims of underdetermination vary in strength,
and he goes on to insist that those who attribute dramatic
significance to the thesis that our scientific theories are
underdetermined by the evidence defend only the weaker versions of
that thesis, yet draw dire consequences and shocking morals regarding
the character and status of the scientific enterprise from much
stronger versions. He suggests, for instance, that Quine's
famous claim that any hypothesis can be preserved "come what
may" in the way of evidence can be defended simply as a
description of what it is *psychologically* possible for human
beings to do, but Laudan insists that in this form the thesis is
simply bereft of interesting or important consequences for
epistemology-- the study of *knowledge*. Along this
dimension of variation, the strong version of the thesis asserts that
it is always normatively or rationally *defensible* to retain
any hypothesis in the light of any evidence whatsoever, but this
latter, stronger version of the claim, Laudan suggests, is one for
which no convincing evidence or argument has ever been offered. More
generally, Lauden argues, arguments for underdetermination turn on
implausibly treating all logically possible responses to the evidence
as equally justified or rationally defensible. For example, Laudan
suggests that we might reasonably hold the resources of *deductive
logic* to be insufficient to single out just one acceptable
response to disconfirming evidence, but not that deductive logic
*plus the sorts of ampliative principles of good reasoning
typically deployed in scientific contexts* are insufficient to do
so. Similarly, defenders of underdetermination might assert the
*nonuniqueness* claim that for any given theory or web of
beliefs, either there is at least one alternative that can also be
reconciled with the available evidence, or the much stronger claim
that *all* of the contraries of any given theory can be
reconciled with the available evidence equally well. And the claim of
such "reconciliation" itself disguises a wide range of
further alternative possibilities: that our theories can be made
*logically compatible* with any amount of disconfirming
evidence (perhaps by the simple expedient of removing any claim(s)
with which the evidence is in conflict), that any theory may be
reformulated or revised so as to *entail* any piece of
previously disconfirming evidence, or so as to *explain*
previously disconfirming evidence, or that any theory can be made to
be *as well supported empirically* by any collection of
evidence as any other theory. And in *all* of these respects,
Laudan claims, partisans have defended only the weaker forms of
underdetermination while founding their further claims about and
conceptions of the scientific enterprise on versions much stronger
than those they have managed or even attempted to defend.



Laudan is certainly right to distinguish these various versions of
holist underdetermination, and he is equally right to suggest that
many of the thinkers he confronts have derived grand morals concerning
the scientific enterprise from much stronger versions of
underdetermination than they are able to defend, but the underlying
situation is somewhat more complex than he suggests. Laudan's
overarching claim is that champions of holist underdetermination show
only that a wide variety of responses to disconfirming evidence are
logically possible (or even just psychologically possible), rather
than that these are all rationally defensible or equally
well-supported by the evidence. But his straightforward appeal to
further epistemic resources like ampliative principles of belief
revision that are supposed to help narrow the merely logical
possibilities down to those which are reasonable or rationally
defensible is itself problematic, at least as part of any attempt to
respond to Quine. This is because on Quine's holist picture of
knowledge such further ampliative principles governing legitimate
belief revision are *themselves* simply part of the web of our
beliefs, and are therefore open to revision in response to
recalcitrant experience as well. Indeed, this is true even for the
principles of deductive logic and the (consequent) demand for
particular forms of logical consistency between parts of the web
itself! So while it is true that the ampliative principles we
currently embrace do not leave all logically or even psychologically
possible responses to the evidence open to us (or leave us free to
preserve any hypothesis "come what may"), our continued
adherence to *these very principles*, rather than being willing
to revise the web of belief so as to abandon them, is part of the
phenomenon to which Quine is using underdetermination to draw our
attention, and so cannot be taken for granted without begging the
question. Put another way, Quine does not simply ignore the further
principles that function to ensure that we revise the web of belief in
one way rather than others, but it follows from his account that such
principles are themselves part of the web and therefore candidates for
revision in our efforts to bring the web of beliefs into conformity
(by the resulting web's own lights) with sensory experience.
This recognition makes clear why it will be extremely difficult to say
how the shift to an alternative web of belief (with alternative
ampliative or even deductive principles of belief revision) should or
even can be evaluated for its rational defensibility. Each proposed
revision is likely to be maximally rational by the lights of the
principles it itself
 sanctions.[5]
 Of course we can rightly say that many candidate revisions would
violate our *presently accepted* ampliative principles of
rational belief revision, but the preference we have for those rather
than the alternatives is itself simply generated by their position in
the web of belief we have inherited, and the role that they themselves
play in guiding the revisions we are inclined to make to that web in
light of ongoing experience.



Thus, if we accept Quine's general picture of knowledge, it
becomes quite difficult to disentangle normative from descriptive
issues, or questions about the psychology of human belief revision
from questions about the justifiability or rational defensibility of
such revisions. It is in part for this reason that Quine famously
suggests (1969, 82; see also p 75-76) that epistemology itself
"falls into place as a chapter of psychology and hence of
natural science." His point is not that epistemology should
simply be abandoned in favor of psychology, but instead that there is
ultimately no way to draw a meaningful distinction between the two.
(James Woodward, in comments on an earlier draft of this entry,
pointed out that this makes it all the harder to assess the
significance of Quinean underdetermination in light of Laudan's
complaint or even know the rules for doing so, but in an important way
this difficulty was Quine's point all along!) Quine's
claim is that "[e]ach man is given a scientific heritage plus a
continuing barrage of sensory stimulation; and the considerations
which guide him in warping his scientific heritage to fit his
continuing sensory promptings are, where rational, pragmatic"
(1951, 46), but the role of these pragmatic considerations or
principles in selecting just one of the many possible revisions of the
web of belief in response to recalcitrant experience is not to be
contrasted with those same principles having rational or epistemic
justification. Far from conflicting with or even being orthogonal to
the search for truth and our efforts to render our beliefs maximally
responsive to the evidence, Quine insists, revising our beliefs in
accordance with such pragmatic principles "at bottom, is what
evidence is" (1955, 251). Whether or not this strongly
naturalistic conception of epistemology can ultimately be defended, it
is misleading for Laudan to suggest that the thesis of
underdetermination becomes trivial or obviously insupportable the
moment we inquire into the rational defensibility rather than the mere
logical or psychological possibility of alternative revisions to the
holist's web of belief.



In fact, there is an important connection between this lacuna in
Laudan's discussion and the further uses made of the thesis of
underdetermination by sociologists of scientific knowledge, feminist
epistemologists, and other vocal champions of holist
underdetermination. When faced with the invocation of further
ampliative standards or principles that supposedly rule out some
responses to disconfirmation as irrational or unreasonable, these
thinkers typically respond by insisting that the embrace of such
further standards or principles (or perhaps their application to
particular cases) is *itself* underdetermined, historically
contingent, and/or subject to ongoing social negotiation. For this
reason, they suggest, such appeals (and their success or failure in
convincing the members of a given community) should be explained by
reference to the same broadly social and political interests that they
claim are at the root of theory choice and belief change in science
more generally (see, e.g., Shapin and Schaffer, 1985). On both
accounts, then, our response to recalcitrant evidence or a failed
prediction is constrained in important ways by features of the
existing web of beliefs. But for Quine, the continuing force of these
constraints is ultimately imposed by the fundamental principles of
human psychology (such as our preference for minimal mutilation of the
web, or the pragmatic virtues of simplicity, fecundity, etc.), while
for constructivist theorists of science such as Shapin and Schaffer,
the continuing force of any such constraints is limited only by the
ongoing negotiated agreement of the communities of scientists who
respect them.



As this last contrast makes clear, recognizing the limitations of
Laudan's critique of Quine and the fact that we cannot dismiss
holist underdetermination with any straightforward appeal to
ampliative principles of good reasoning by itself does nothing to
establish the further *positive* claims about belief revision
advanced by interest-driven theorists of science. Conceding that
theory choice or belief revision in science is underdetermined by the
evidence in just the ways that Duhem and/or Quine suggested leaves
entirely open whether it is instead the (suitably broad) social or
political interests of scientists themselves that do the further work
of singling out the particular beliefs or responses to falsifying
evidence that any particular scientist or scientific community will
actually adopt or find compelling. Even many of those philosophers of
science who are most strongly convinced of the general significance of
various forms of underdetermination remain deeply skeptical of this
latter thesis and thoroughly unconvinced by the empirical evidence
that has been offered in support of it (usually in the form of case
studies of particular historical episodes in science).



Appeals to underdetermination have also loomed large in recent
philosophical debates concerning the place of values in science, with
a number of authors arguing that the underdetermination of theory by
data is among the central reasons that values (or
"non-epistemic" values) do and perhaps must play a central
role in scientific inquiry. Feminist philosophers of science have
sometimes suggested that it is such underdetermination which creates
room not only for unwarranted androcentric values or assumptions to
play central roles in the embrace of particular theoretical
possibilities, but also for the critical and alternative approaches
favored by feminists themselves (e.g. Nelson 2022). But appeals to
underdetermination also feature prominently in more general arguments
against the possibility or desirability of value-free science. Perhaps
most influentially, Helen Longino's "contextual
empiricism" suggests that a wide variety of non-epistemic values
play important roles in determining our scientific beliefs in part
because underdetermination prevents data or evidence alone from doing
so. For this and other reasons she concludes that objectivity in
science is therefore best served by a diverse set of participants who
bring a variety of different values or value-laden assumptions to the
enterprise (Longino 1990, 2002).


## 3. Contrastive Underdetermination, Empirical Equivalents, and Unconceived Alternatives


### 3.1 Contrastive Underdetermination: Back to Duhem



Although it is also a form of underdetermination, what we described in
Section 1 above as contrastive underdetermination raises fundamentally
different issues from the holist variety considered in Section 2 (Bonk
2008 raises many of these issues). John Stuart Mill articulated the
challenge of contrastive underdetermination with impressive clarity in
*A System of Logic*, where he writes:



> 
> Most thinkers of any degree of sobriety allow, that an hypothesis...is
> not to be received as probably true because it accounts for all the
> known phenomena, since this is a condition sometimes fulfilled
> tolerably well by two conflicting hypotheses...while there are
> probably a thousand more which are equally possible, but which, for
> want of anything analogous in our experience, our minds are unfitted
> to conceive. ([1867] 1900, 328)
> 



This same concern is also evident in Duhem's original writings
concerning so-called crucial experiments, where he seeks to show that
even when we explicitly suspend any concerns about holist
underdetermination, the contrastive variety remains an obstacle to our
discovery of truth in theoretical science:



> 
> But let us admit for a moment that in each of these systems
> [concerning the nature of light] everything is compelled to be
> necessary by strict logic, except a single hypothesis; consequently,
> let us admit that the facts, in condemning one of the two systems,
> condemn once and for all the single doubtful assumption it contains.
> Does it follow that we can find in the 'crucial
> experiment' an irrefutable procedure for transforming one of the
> two hypotheses before us into a demonstrated truth? Between two
> contradictory theorems of geometry there is no room for a third
> judgment; if one is false, the other is necessarily true. Do two
> hypotheses in physics ever constitute such a strict dilemma? Shall we
> ever dare to assert that no other hypothesis is imaginable? Light may
> be a swarm of projectiles, or it may be a vibratory motion whose waves
> are propagated in a medium; is it forbidden to be anything else at
> all? ([1914] 1954, 189)
> 



Contrastive underdetermination is so-called because it questions the
ability of the evidence to confirm any given hypothesis *against
alternatives*, and the central focus of discussion in this
connection (equally often regarded as "the" problem of
underdetermination) concerns the character of the supposed
alternatives. Of course the two problems are not entirely
disconnected, because it is open to us to consider alternative
possible modifications of the web of beliefs as alternative theories
between which the empirical evidence alone is powerless to decide. But
we have already seen that one *need* not think of the
alternative responses to recalcitrant experience as competing
theoretical alternatives to appreciate the character of the
holist's challenge, and we will see that one need not embrace
any version of holism about confirmation to appreciate the quite
distinct problem that the available evidence might support more than
one theoretical alternative. It is perhaps most useful here to think
of holist underdetermination as starting from a particular theory or
body of beliefs and claiming that our revision of those beliefs in
response to new evidence may be underdetermined, while contrastive
underdetermination instead starts from a given body of evidence and
claims that more than one theory may be well-supported by that
evidence. Part of what has contributed to the conflation of these two
problems is the holist presuppositions of those who originally made
them famous. After all, on Quine's view, we simply revise the
web of belief in response to recalcitrant experience, and so the
suggestion that there are multiple possible revisions of the web
available in response to any particular evidential finding just
*is* the claim that there are in fact many different
"theories" (i.e. candidate webs of belief) that are
equally well-supported by any given body of
 data.[6]
 But if we give up such extreme holist views of evidence, meaning,
and/or confirmation, the two problems take on very different
identities, with very different considerations in favor of taking them
seriously, very different consequences, and very different candidate
solutions. Notice, for instance, that even if we somehow knew that no
other hypothesis on a given subject was well-confirmed by a given body
of data, that would not tell us where to place the blame or which of
our beliefs to give up if the remaining hypothesis in conjunction with
others subsequently resulted in a failed empirical prediction. And as
Duhem suggests in the passage cited above, even if we supposed that we
somehow knew exactly which of our hypotheses to blame in response to a
failed empirical prediction, this would not help us to decide whether
or not there are other hypotheses available that are also
well-confirmed by the data we actually have.



One way to see why not is to consider an analogy that champions of
contrastive underdetermination have sometimes used to support their
case. If we consider any finite group of data points, an elementary
proof reveals that there are an infinite number of distinct
mathematical functions describing different curves that will pass
through all of them. As we add further data to our initial set we will
eliminate functions describing curves which no longer capture all of
the data points in the new, larger set, but no matter how much data we
accumulate, there will always be an infinite number of functions
*remaining* that define curves including all the data points in
the new set and which would therefore seem to be equally well
supported by the empirical evidence. *No* finite amount of data
will *ever* be able to narrow the possibilities down to just a
single function or indeed, any finite number of candidate functions,
from which the distribution of data points we have might have been
generated. Each new data point we gather eliminates an infinite number
of curves that *previously* fit all the data (so the problem
here is not the holist's challenge that we do not know which
beliefs to give up in response to failed predictions or disconfirming
evidence), but also leaves an infinite number still in contention.


### 3.2 Empirically Equivalent Theories



Of course, generating and testing fundamental scientific hypotheses is
rarely if ever a matter of finding curves that fit collections of data
points, so nothing follows directly from this mathematical analogy for
the significance of contrastive underdetermination in most scientific
contexts. But Bas van Fraassen has offered an extremely influential
line of argument intended to show that such contrastive
underdetermination is a serious concern for scientific theorizing more
generally. In *The Scientific Image* (1980), van Fraassen uses
a now-classic example to illustrate the possibility that even our best
scientific theories might have *empirical equivalents*: that
is, alternative theories making the very same empirical predictions,
and which therefore cannot be better or worse supported by any
*possible* body of evidence. Consider Newton's cosmology,
with its laws of motion and gravitational attraction. As Newton
himself realized, exactly the same predictions are made by the theory
whether we assume that the entire universe is at rest or assume
instead that it is moving with some constant velocity in any given
direction: from our position within it, we have no way to detect
constant, absolute motion by the universe as a whole. Thus, van
Fraassen argues, we are here faced with empirically equivalent
scientific theories: Newtonian mechanics and gravitation conjoined
either with the fundamental assumption that the universe is at
absolute rest (as Newton himself believed), or with any one of an
infinite variety of alternative assumptions about the constant
velocity with which the universe is moving in some particular
direction. All of these theories make all and only the same empirical
predictions, so no evidence will ever permit us to decide between them
on empirical
 grounds.[7]



Van Fraassen is widely (though mistakenly) regarded as holding that
the prospect of contrastive underdetermination grounded in such
empirical equivalents demands that we restrict our epistemic ambitions
for the scientific enterprise itself. His constructive empiricism
holds that the aim of science is not to find true theories, but only
theories that are empirically adequate: that is, theories whose claims
about *observable phenomena* are all true. Since the empirical
adequacy of a theory is not threatened by the existence of another
that is empirically equivalent to it, fulfilling this aim has nothing
to fear from the possibility of such empirical equivalents. In reply,
many critics have suggested that van Fraassen gives no reasons for
restricting belief to empirical adequacy that could not also be used
to argue for suspending our belief in the *future* empirical
adequacy of our best present theories. Of course there *could*
be empirical equivalents to our best theories, but there could also be
theories equally well-supported by all the evidence up to the present
which diverge in their predictions about observables in future cases
not yet tested. This challenge seems to miss the point of van
Fraassen's epistemic voluntarism: his claim is that we should
believe no more *but also no less* than we need to take full
advantage of our scientific theories, and a commitment to the
empirical adequacy of our theories, he suggests, is the least we can
get away with in this regard. Of course it is true that we are running
some epistemic risk in believing in even the full empirical adequacy
of our present theories, but this is the minimum we need to take full
advantage of the fruits of our scientific labors, and the risk is
considerably less than what we assume in believing in their truth: as
van Fraassen famously suggests, "it is not an epistemic
principle that one might as well hang for a sheep as a lamb"
(1980, 72).



In an influential discussion, Larry Laudan and Jarrett Leplin (1991)
argue that philosophers of science have invested even the bare
possibility that our theories might have empirical equivalents with
far too much epistemic significance. Notwithstanding the popularity of
the presumption that there are empirically equivalent rivals to every
theory, they argue, the conjunction of several familiar and relatively
uncontroversial epistemological theses is sufficient to defeat it.
Because the boundaries of what is observable change as we develop new
experimental methods and instruments, because auxiliary assumptions
are always needed to derive empirical consequences from a theory (cf.
confirmational holism, above), and because these auxiliary assumptions
are themselves subject to change over time, Laudan and Leplin conclude
that there is no guarantee that any two theories judged to be
empirically equivalent at a given time will remain so as the state of
our knowledge advances. Accordingly, any judgment of empirical
equivalence is both defeasible and relativized to a particular state
of science. So even if two theories are empirically equivalent at a
given time this is no guarantee that they will *remain* so, and
thus there is no foundation for a general pessimism about our ability
to distinguish theories that are empirically equivalent to each other
on empirical grounds. Although they concede that we could have good
reason to think that particular theories have empirically equivalent
rivals, this must be established case-by-case rather than by any
general argument or presumption.



One fairly standard reply to this line of argument is to suggest that
what Laudan and Leplin really show is that the notion of empirical
equivalence must be applied to larger collections of beliefs than
those traditionally identified as scientific theories--at least
large enough to encompass the auxiliary assumptions needed to derive
empirical predictions from them. At the extreme, perhaps this means
that the notion of empirical equivalents (or at least timeless
empirical equivalents) cannot be applied to anything less than
"systems of the world" (i.e. total Quinean webs of
belief), but even that is not fatal: what the champion of contrastive
underdetermination asserts is that there are empirically equivalent
systems of the world that *incorporate* different theories of
the nature of light, or spacetime, or whatever (for useful discussion,
see Okasha 2002). On the other hand, it might seem that quick examples
like van Fraassen's variants of Newtonian cosmology do not serve
to make *this* thesis as plausible as the more limited claim of
empirical equivalence for individual theories. It seems equally
natural, however, to respond to Laudan and Leplin simply by conceding
the variability in empirical equivalence but insisting that this is
not enough to undermine the problem. Empirical equivalents create a
serious obstacle to belief in a theory so long as there is
*some* empirical equivalent to that theory at any given time,
but it need not be the same one at each time. On this line of
thinking, cases like van Fraassen's Newtonian example illustrate
how easy it is for theories to admit of empirical equivalents at any
given time, and thus constitute a reason for thinking that there
probably are or will be empirical equivalents to any given theory at
any particular time, assuring that whenever the question of belief in
a given theory arises, the challenge posed to it by contrastive
underdetermination arises as well.



Laudan and Leplin also suggest, however, that even if the universal
existence of empirical equivalents were conceded, this would do much
less to establish the significance of underdetermination than its
champions have supposed, because "theories with exactly the same
empirical consequences may admit of differing degrees of evidential
support" (1991, 465). A theory may be better supported than an
empirical equivalent, for instance, because the former but not the
latter is derivable from a more general theory whose consequences
include a third, well supported, hypothesis. More generally, the
belief-worthiness of an hypothesis depends crucially on how it is
connected or related to other things we believe and the evidential
support we have for those other
 beliefs.[8]
 Laudan and Leplin suggest that we have invited the specter of rampant
underdetermination only by failing to keep this familiar home truth in
mind and instead implausibly identifying the evidence bearing on a
theory exclusively with the theory's own entailments or
empirical consequences (but cf. Tulodziecki 2012). This impoverished
view of evidential support, they argue, is in turn the legacy of a
failed foundationalist and positivistic approach to the philosophy of
science which mistakenly assimilates epistemic questions about how to
decide whether or not to believe a theory to semantic questions about
how to establish a theory's meaning or truth-conditions.



John Earman (1993) has argued that this dismissive diagnosis does not
do justice to the threat posed by underdetermination. He argues that
worries about underdetermination are an aspect of the more general
question of the reliability of our inductive methods for determining
beliefs, and notes that we cannot decide how serious a problem
underdetermination poses without specifying (as Laudan and Leplin do
not) the inductive methods we are considering. Earman regards some
version of Bayesianism as our most promising form of inductive
methodology, and he proceeds to show that challenges to the long-run
reliability of our Bayesian methods can be motivated by considerations
of the empirical indistinguishability (in several different and
precisely specified senses) of hypotheses stated in any language
richer than that of the evidence itself that do not amount simply to
general skepticism about those inductive methods. In other words, he
shows that there are more reasons to worry about underdetermination
concerning inferences to hypotheses about unobservables than to, say,
inferences about unobserved observables. He also goes on to argue that
at least two genuine cosmological theories have serious, nonskeptical,
and nonparasitic empirical equivalents: the first essentially replaces
the gravitational field in Newtonian mechanics with curvature in
spacetime itself,
 [9]
 while the second recognizes that Einstein's General Theory of
Relativity permits cosmological models exhibiting different global
topological features which cannot be distinguished by any evidence
inside the light cones of even idealized observers who live
 forever.[10]
 And he suggests that "the production of a few concrete examples
is enough to generate the worry that only a lack of imagination on our
part prevents us from seeing comparable examples of underdetermination
all over the map" (1993, 31) even as he concedes that his case
leaves open just how far the threat of underdetermination extends
(1993, 36).



Most philosophers of science, however, have not embraced the idea that
it is only lack of imagination which prevents us from finding
empirical equivalents to our scientific theories generally. They note
that the convincing examples of empirical equivalents we do have are
all drawn from a single domain of highly mathematized scientific
theorizing in which the background constraints on serious theoretical
alternatives are far from clear, and suggest that it is therefore
reasonable to ask whether even a small handful of such examples should
make us believe that there are probably empirical equivalents to most
of our scientific theories most of the time. They concede that it is
always *possible* that there are empirical equivalents to even
our best scientific theories concerning any domain of nature, but
insist that we should not be willing to suspend belief in any
*particular* theory until some convincing alternative to it can
actually be produced: as Philip Kitcher puts it, "give us a
rival explanation, and we'll consider whether it is sufficiently
serious to threaten our confidence" (1993, 154; see also Leplin
1997, Achinstein 2002). That is, these thinkers insist that until we
are able to *actually construct* an empirically equivalent
alternative to a given theory, the bare possibility that such
equivalents exist is insufficient to justify suspending belief in the
best theories we do have. For this same reason most philosophers of
science are unwilling to follow van Fraassen into what they regard as
constructive empiricism's unwarranted epistemic modesty. Even if
van Fraassen is right about the most minimal beliefs we must hold in
order to take full advantage of our scientific theories, most thinkers
do not see why we should believe the least we can get away with rather
than believing the most we are entitled to by the evidence we
have.



Champions of contrastive underdetermination have most frequently
responded by trying to establish that *all* theories have
empirical equivalents, typically by proposing something like an
algorithmic procedure for generating such equivalents from any theory
whatsoever. Stanford (2001, 2006) suggests that these efforts to
*prove* that all our theories must have empirical equivalents
fall roughly but reliably into global and local varieties, and that
neither makes a convincing case for a distinctive scientific problem
of contrastive underdetermination. Global algorithms are
well-represented by Andre Kukla's (1996) suggestion that from
any theory *T* we can immediately generate such empirical
equivalents as *T*' (the claim that *T*'s
observable consequences are true, but *T* itself is false),
*T*'' (the claim that the world behaves according to
*T* when observed, but some specific incompatible alternative
otherwise), and the hypothesis that our experience is being
manipulated by powerful beings in such a way as to make it appear that
*T* is true. But such possibilities, Stanford argues, amount to
nothing more than the sort of Evil Deceiver to which Descartes
appealed in order to doubt any of his beliefs that could possibly be
doubted (see Section 1, above). Such radically skeptical scenarios
pose an equally powerful (or powerless) challenge to any knowledge
claim whatsoever, no matter how it is arrived at or justified, and
thus pose no *special* problem or challenge for beliefs offered
to us by theoretical science. If global algorithms like Kukla's
are the only reasons we can give for taking underdetermination
seriously in a scientific context, then there is no distinctive
problem of the underdetermination of scientific theories by data, only
a salient reminder of the irrefutability of classically Cartesian or
radical
 skepticism.[11]



In contrast to such global strategies for generating empirical
equivalents, local algorithmic strategies instead begin with some
particular scientific theory and proceed to generate alternative
versions that will be equally well supported by all possible evidence.
This is what van Fraassen does with the example of Newtonian
cosmology, showing that an infinite variety of supposed empirical
equivalents can be produced by ascribing different constant absolute
velocities to the universe as a whole. But Stanford suggests that
empirical equivalents generated in this way are also insufficient to
show that there is a distinctive and genuinely troubling form of
underdetermination afflicting scientific theories, because they rely
on simply saddling particular scientific theories with further claims
for which those theories themselves (together with whatever background
beliefs we actually hold) imply that we cannot have any evidence. Such
empirical equivalents invite the natural response that they simply
tack on to our theories further commitments that are or should be no
part of those theories themselves. Such claims, it seems, should
simply be excised from our theories, leaving over just the claims that
sensible defenders would have held were all we were entitled to
believe by the evidence in any case. In van Fraassen's Newtonian
example, for instance, this could be done simply by undertaking no
commitment concerning the absolute velocity and direction (or lack
thereof) of the universe as a whole. Note also that if we believe a
given scientific theory when one of the empirical equivalents we could
generate from it by the local algorithmic strategy is correct instead,
most of what we originally believed will nonetheless turn out to be
straightforwardly true.

 Philosophers of science have responded in
a variety of ways to the suggestion that a few or even a small handful
of serious examples of empirical equivalents does not suffice to
establish that there are probably such equivalents to most scientific
theories in most domains of inquiry. One such reaction has been to
invite more careful attention to the details of particular examples of
putative underdetermination: considerable work has been devoted to
assessing the threat of underdetermination in the case of particular
scientific theories (for recent examples see Pietsch 2012; Tulodziecki
2013; Werndl 2013; Belot 2014; Butterfield 2014; Miyake 2015; Kovaka
2019; Fletcher 2021, and others). Other thinkers have sought to
investigate whether certain types of scientific theories or theories
in particular scientific fields differ in the extent to which they are
genuinely threatened by underdetermination. Some have argued that
underdetermination poses a less serious (Cleland 2002; Carman 2005) or
a more serious (Turner 2005, 2007) challenge for
'historical' sciences like geology, paleontology, and
archaeology than it does for 'experimental' sciences like
particle physics. Others have resisted such generalizations but
nonetheless argued that underdetermination predicaments arise in
distinctive or characteristic ways in historical sciences and that
scientists in these fields have different resources and strategies for
addressing them (Currie 2018; Forber and Griffith 2011; Stanford
2010). Finally, some thinkers have sought to defend particular forms
of explanation frequently deployed in historical sciences, such as
narrative explanation (Sterelny and Currie 2017), from the charge that
they suffer from rampant underdetermination.

### 3.3 Unconceived Alternatives and A New Induction



Stanford (2001, 2006) concludes that no convincing general case has
been made for the presumption that there are empirically equivalent
rivals to all or most scientific theories, or to any theories besides
those for which such equivalents can actually be constructed. But he
goes on to insist that empirical equivalents are no essential part of
the case for a significant problem of contrastive underdetermination.
Our efforts to confirm scientific theories, he suggests, are no less
threatened by what Larry Sklar (1975, 1981) has called
"transient" underdetermination, that is, theories which
are *not* empirically equivalent but are equally (or at least
reasonably) well confirmed by all the evidence we happen to have in
hand at the moment, so long as this transient predicament is also
"recurrent", that is, so long as we think that there is
(probably) at least one such (fundamentally distinct) alternative
available--and thus the transient predicament
re-arises--whenever we are faced with a decision about whether to
believe a given theory at a given time. Stanford argues that a
convincing case for contrastive underdetermination of this recurrent,
transient variety can indeed be made, and that the evidence for it is
available in the historical record of scientific inquiry itself.



Stanford concedes that present theories are not transiently
underdetermined by the theoretical alternatives we have actually
developed and considered to date: we think that our own scientific
theories are considerably better confirmed by the evidence than any
rivals we have actually produced. The central question, he argues, is
whether we should believe that there are well confirmed alternatives
to our best scientific theories that are *presently
unconceived* by us. And the primary reason we should believe that
there are, he claims, is the long history of repeated transient
underdetermination by *previously* unconceived alternatives
across the course of scientific inquiry. In the progression from
Aristotelian to Cartesian to Newtonian to contemporary mechanical
theories, for instance, the evidence available at the time each
earlier theory dominated the practice of its day also offered
compelling support for each of the later alternatives (unconceived at
the time) that would ultimately come to displace it. Stanford's
"New Induction" over the history of science claims that
this situation is typical; that is, that "we have, throughout
the history of scientific inquiry and in virtually every scientific
field, repeatedly occupied an epistemic position in which we could
conceive of only one or a few theories that were well confirmed by the
available evidence, while subsequent inquiry would routinely (if not
invariably) reveal further, radically distinct alternatives as well
confirmed by the previously available evidence as those we were
inclined to accept on the strength of that evidence" (2006, 19).
In other words, Stanford claims that in the past we have repeatedly
failed to exhaust the space of fundamentally distinct theoretical
possibilities that were well confirmed by the existing evidence, and
that we have every reason to believe that we are probably also failing
to exhaust the space of such alternatives that are well confirmed by
the evidence we have at present. Much of the rest of his case is taken
up with discussing historical examples illustrating that earlier
scientists did not simply ignore or dismiss, but instead genuinely
*failed to conceive of* the serious, fundamentally distinct
theoretical possibilities that would ultimately come to displace the
theories they defended, only to be displaced in turn by others that
were similarly unconceived at the time. He concludes that "the
history of scientific inquiry itself offers a straightforward
rationale for thinking that there typically are alternatives to our
best theories equally well confirmed by the evidence, even when we are
unable to conceive of them at the time" (2006, 20; for
reservations and criticisms concerning this line of argument, see
Magnus 2006, 2010; Godfrey-Smith 2008; Chakravartty 2008; Devitt 2011;
Ruhmkorff 2011; Lyons 2013). Stanford concedes, however, that the
historical record can offer only fallible evidence of a distinctive,
general problem of contrastive scientific underdetermination, rather
than the kind of deductive proof that champions of the case from
empirical equivalents have typically sought. Thus, claims and
arguments about the various forms that underdetermination may take,
their causes and consequences, and the further significance they hold
for the scientific enterprise as a whole continue to evolve in the
light of ongoing controversy, and the underdetermination of scientific
theory by evidence remains very much a live and unresolved issue in
the philosophy of science.