## 1. The History of the Historical Challenge


### 1.1 The Bankruptcy-of-science Debate



The issue of theory-change in science was debated in the context of
the 'bankruptcy of science' controversy that was raging in
Paris in the last decade of the nineteenth century and the first
decade of the twentieth. A claim of growing popular reputation among
various public intellectuals, spearheaded by Ferdinand
Brunetiere and Leo Tolstoy, was that scientific theories are
ephemeral; and this was supposed to prove that science has at best no
more than predictive value with no legitimate claim to showing what
the world is like--especially in its unobservable aspects. In
light of a growing interest in the history of science among scientists
and philosophers, it was pointed out that science has had a poor track
record: it has gone through many radical theory-changes in the past;
hence, there is reason to believe that what is *currently*
accepted will be overturned in the future.



In his essay "The Non-Acting", published in French in
August 1893, the Russian novelist Tolstoy (1828-1910) noted:



> 
> 
> Lastly, does not each year produce its new scientific discoveries,
> which after astonishing the boobies of the whole world and bringing
> fame and fortune to the inventors, are eventually admitted to be
> ridiculous mistakes even by those who promulgated them? (...)
> Unless then our century forms an exception (which is a supposition we
> have no right to make), it needs no great boldness to conclude by
> analogy that among the kinds of knowledge occupying the attention of
> our learned men and called science, there must necessarily be some
> which will be regarded by our descendants much as we now regard the
> rhetoric of the ancients and the scholasticism of the Middle Ages.
> (1904: 105)
> 
> 
> 



A few years earlier, in 1889, Ferdinand Brunetiere
(1849-1906), Professor at the *Ecole Normale
Superieure* and editor of the prestigious journal *Revue
des Deux Mondes*, noted in his review of Paul Bourget's play
'*Le Disciple*':



> 
> 
> We differ from animals in recognizing that humans have to be first
> (i.e., they have value). The laws of nature, the 'struggle for
> life' or 'natural selection', do not show what we
> have in common. Are these the only laws? Do we know whether perhaps
> tomorrow they will not join in the depths of oblivion the Cartesian
> vortices or the 'quiddities' of scholasticism? (1889: 222,
> author's translation)
> 
> 
> 



This history-fed pessimism about science, which seemed to capture the
public mood, led to a spirited reaction by the scientific community.
In an anonymous article that appeared in *Revue Scientifique*,
a prestigious semi-popular scientific journal, in August 17 1889, the
following questions were raised: Is the history of science the history
of human error? Will what theories affirm today be affirmed in a
century or two? The reply was:



> 
> 
> We will say to savants, philosophers and physicists, physicians,
> chemists, astronomers or geologists: Go forward boldly, without
> looking behind you, without caring for the consequences, reasonable or
> absurd, that can be drawn from your work. Seek the truth, without the
> worry of its applications. (Anonymous 1889: 215, author's
> translation)
> 
> 
> 



A few years later, in 1895, Brunetiere strikes back with an
article titled '*Apres Une Visite Au
Vatican*', published in *Revue des Deux Mondes*, by
claiming that science is bankrupt:



> 
> 
> Science has failed to deliver on its promise to change 'the face
> of the world'. (...) Even if this is not a total bankruptcy, it
> is certainly a partial bankruptcy, enough to shake off the credit from
> science. (1895: 98, 103)
> 
> 
> 



The eminent scientist Charles Richet (1850-1935), Professor of
Physiology at the College de France, Editor of *Revue
Scientifique* and Nobel Laureate for Medicine in 1913, replied
with an article titled *'La Science a-t-elle fait
banqueroute?'* (*Revue Scientifique*, 12 January
1895), which appeared in the section: *Histoire des Sciences*.
In this, he did three things. Firstly, he noted that science can never
understand the 'why' ('*le pourquoi*')
of things, especially when it comes to the infinitely small and the
infinitely large. Science "attends only to the phenomena. The
intimate nature of things escapes from us" (1895: 34). Secondly,
he stressed that "science has not promised anything", let
alone the discovery of the essence of things. Thirdly, he added that
despite the fact that science has made no promises, it has changed the
world, citing various scientific, industrial and technological
successes (from the invention of printing and the microscope to the
railways, the electric battery, the composition of the air, and the
nature of fermentation).



Turning Brunetiere's argument on its head, Richet
formulated what might be called an 'optimistic induction'
based on the then recent history of scientific successes. To those who
claim that science has failed in the past, his reply is that history
shows that it is unreasonable to claim for any scientific question
that we will always fail to answer it. Far from warranting epistemic
pessimism, the history of science is a source of cognitive optimism.
Richet referred to a few remarkable cases, the most striking of which
is the case of Jean Louis Prevost and Jean Baptiste Dumas, who had
written in 1823:



> 
> 
> The pointlessness of our attempts to isolate the colouring matter of
> the blood gives us almost the certainty that one will never be able to
> find it. (1823, 246, author's translation)
> 
> 
> 



Forty years after their bold statement, Richet exclaimed, this
coloured matter (haemoglobin) had been isolated, analysed and
studied.



Richet's reply to the historical challenge suggested lowering
the epistemic bar for science: science describes the phenomena and
does not go beyond them to their (unobservable) causes. This attitude
was echoed in the reply to the 'bankruptcy charge' issued
by the eminent chemist and politician of the French Third Republic,
Marcelin Berthelot (1827-1907) in his pamphlet *Science et
Morale* in 1897. He was firm in his claim that the alleged
bankruptcy of science is an illusion of the non-scientific mind. Like
Richet, he also argued that science has not pretended to have
penetrated into the essence of things: "under the words
'essence', 'the nature of things', we hide the
idols of our own imagination" (1897: 18, author's
translation). Science, he noted, has as its starting point the study
of facts and aims to establish general relations, that is,
'scientific laws', on their basis. If science does not aim
for more, we cannot claim that it is bankrupt; we cannot accuse it for
"affirmations it did not make, or hopes it has not
 aroused".[1]



Berthelot, who objected to atomism, captured a broad positivist trend
in French science at the end of the nineteenth century, according to
which science cannot offer knowledge of anything other than the
phenomena. In light of this view, the history-fed pessimism is
misguided precisely because there has been substantial continuity at
the level of the description of the phenomena, even if explanatory
theories have come and gone.


### 1.2 Duhem on Continuity



This kind of attitude was captured by Pierre Duhem's (1906)
distinction between two parts of a scientific theory: the
representative part, which classifies a set of experimental laws; and
the explanatory part, which "takes hold of the reality
underlying the phenomena" (1906 [1954: 32]). Duhem understood
the representative part of a theory as comprising the empirical laws
and the mathematical formalism, which is used to represent,
systematize and correlate these laws, while he thought that the
explanatory part relates to the construction of physical (and in
particular, mechanical) models and explanatory hypotheses about the
nature of physical processes which purport to reveal underlying
unobservable causes of the phenomena. For him, the explanatory part is
parasitic on the representative. To support this view, he turned to
the history of science, especially the history of optical theories and
of mechanics. He argued that when a theory is abandoned because it
fails to cover new experimental facts and laws, its representative
part is retained, partially or fully, in its successor theory, while
the attempted explanations offered by the theory get abandoned. He
spoke of the "constant breaking-out of explanations which arise
to be quelled" (1906 [1954: 33]).



Though Duhem embedded this claim for continuity in theory-change in an
instrumentalist account of scientific theories, he also took it that
science aims at a natural classification of the phenomena, where a
classification (that is the representation of the phenomena within a
mathematical system) is *natural* if the relations it
establishes among the phenomena gathered by experiments
"correspond to real relations among things" (1906 [1954:
26-27]). Hence, scientific knowledge does go beyond the
phenomena but in doing so, that is, in tending to be a natural
classification, it can extend only up to relations among "hidden
realities whose essence cannot be grasped" (1906 [1954: 297]). A
clear mark of the naturalness of a classification is when it issues in
*novel predictions* (1906 [1954: 28]). Hence, successful novel
predictions issued by a theory are a mark for the theory getting some
aspects of reality right, viz. real relations among unobservable
 entities.[2]


### 1.3 Poincare's Relationism



This kind of relationism became a popular middle way between
positivism and what may be called full-blown realism. Duhem himself,
justly, traced it back to his contemporary Henri Poincare. He
noted with approval that Poincare "felt a sort of
revolt" against the proposition that "theoretical physics
is a mere collection of recipes" and he "loudly proclaimed
that a physical theory gives us something else than the mere knowledge
of the facts, that it makes us discover the real relations among
things ([1906] 2007: 446; improved translation from the French
original by Marie Guegeun and the author).



In his address to the 1900 International Congress of Physics in Paris,
Poincare made a definitive intervention in the
bankruptcy-of-science debate and its history-fed pessimism. He
described the challenge thus:



> 
> 
> The people of world [*les gens du monde*] are struck to see how
> ephemeral scientific theories are. After some years of prosperity,
> they see them successively abandoned; they see ruins accumulated on
> ruins; they predict that the theories in fashion today will quickly
> succumb in their turn, and they conclude that they are absolutely
> futile. This is what they call *the bankruptcy of science*
> (1900: 14, author's translation).
> 
> 
> 



The view of 'the people of the world' is not right:



> 
> 
> Their scepticism is superficial; they understand none of the aim and
> the role of scientific theories; otherwise they would understand that
> ruins can still be good for something.
> 
> 
> 



But unlike the positivist trend around him, Poincare took it
that scientific theories offer knowledge of the relational structure
of the world behind the phenomena. In the Introduction to *La
Science et l'Hypothese* in 1902, he made clear what
he took to be the right answer to the historical challenge:



> 
> 
> Without doubt, at first, the theories seem to us fragile, and the
> history of science proves to us how ephemeral they are; yet they do
> not entirely perish, and of each of them something remains. It is this
> something we must seek to unravel, since there and there alone is the
> true reality. (1902: 26, author's translation)
> 
> 
> 



Poincare argued that what survives in theory-change are
relations among physical magnitudes, expressed by mathematical
equations within theories. His prime example was the reproduction of
Fresnel's laws concerning the relations of amplitudes of
reflected rays vis-a-vis the amplitude of incident rays in the
interface of two media within Maxwell's theory of
electromagnetism, although in this transition, the interpretation of
these laws changed dramatically, from an ether-based account to an
electromagnetic-field-based account. For Poincare



> 
> 
> These equations express relations, and if the equations remain true it
> is because these relations preserve their reality. They teach us,
> before and after, that there is such and such a relation between some
> thing and some other thing; only this something we used to call
> *motion*, we now call it *electric current*. But these
> names were only images substituted for the real objects which nature
> will eternally hide from us. The true relations between these real
> objects are the only reality we can attain to, and the only condition
> is that the same relations exist between these objects as between the
> images by which we are forced to replace them. If these relations are
> known, what does it matter if we deem it convenient to replace one
> image by another? (1900: 15, author's translation.
> 
> 
> 



In recent literature, Poincare's line of thought has come
to be known as *structural realism*, though it may be best if
we describe it as 'relationism'. In the Introduction to
*La Science et l'Hypothese*, he noted that



> 
> 
> the things themselves are not what it [science] can reach, as the
> naive dogmatists think, but only the relations between things. Apart
> from these relations there is no knowable reality. (1902: 25,
> author's translation)
> 
> 
> 



It should be stressed that Poincare does not deny that there is
reality outside relations; but he does deny that this reality is
*knowable*. Note also that Poincare does not use the
expression 'things in themselves' (*choses en soi*)
but the expression 'things themselves' (*chose
elles-memes*). Elsewhere he talks about the "nature of
things" or "real objects". It is quite clear that he
wanted to draw a distinction between how things are--what their
*nature* is--and how they are related to each other (and
to us *qua* knowers). A plausible way to draw this distinction
is to differentiate between the intrinsic and perhaps fully
qualitative properties of things--what he plausibly calls
'nature' of things--and their relations. The former
are unknowable, whereas the latter are
 knowable.[3]



So, Poincare and Duhem initiated a strategy for dealing with
theory-change in science which pointed to substantial continuities
among successive theories. For them, the continuity is, by and large,
relational (and in this sense *mathematical*). Hence,
mathematically-convergent scientific theories reveal the relational
structure of the world.


### 1.4 Boltzmann Against Historical Pessimism



This relational answer to historical pessimism was motivated, at least
partly, by the widespread scepticism towards the atomic theory of
matter. Atomism posited the existence of unobservable
entities--the atoms--to account for a host of observable
phenomena (from chemical bonding to Brownian motion). A trend among
scientists opposed to the explanation of the visible in terms of the
invisible was what Ludwig Boltzmann called
"phenomenologists" (which included the early Max Planck),
according to whom the aim of science was to "write down for
every group of phenomena the equations by means of which their
behavior could be quantitatively calculated" (Boltzmann 1901:
249). The theoretical hypotheses from which the equations might have
been deduced were taken to be the scaffolding that was discarded after
the equations were arrived at. For phenomenologists, then, hypotheses
are not unnecessary or useless--rather they have only a
*heuristic* value: they lead to stable (differential) equations
and *that's it*.



According to Boltzmann, a motivation for this phenomenological
attitude was the "historical principle", viz., that
hypotheses are essentially insecure because they tend to be abandoned
and replaced by others, "totally different" ones. As he
put it:



> 
> 
> frequently opinions which are held in the highest esteem have been
> supplanted within a very short space of time by totally different
> theories; nay, even as St. Remigius the heathens, so now they [the
> phenomenologists] exhorted the theoretical physicists to consign to
> the flames the idols that but a moment previously they had worshipped
> (1901: 252-253).
> 
> 
> 



Like Poincare, Boltzmann's answer to historical pessimism
was that despite the presence of "revolutions" in science,
there is enough continuity in theory change to warrant the claim that
some "achievements may possibly remain the possession of science
for all time" (1901: 253). But unlike Poincare, Boltzmann
did not restrict the criterion of invariance-in-theory-change to
relations only: *The answer to the historical challenge is to look
for patterns of continuity in theory change*. In fact, as
Boltzmann noted, if the historical principle is correct at all, it
cuts also against the equations of the phenomenologists. For unless
these very equations remain invariant through theory-change, there
should be no warrant for taking them to be accurate descriptions of
worldly relations (cf. 1901: 253). Besides, Boltzmann noted, the very
construction of the differential equations of the phenomenologists
requires commitment to substantive atomistic assumptions. Hence, the
phenomenologists are not merely disingenuous when they jettison the
atomistic assumptions after the relevant differential equations have
been arrived at. Their move is self-undermining. In light of the
historical principle, the success of the mathematical equations would
lead to their defeat, since the very theory that led to this success
would fall foul of the historical principle: it would have to be
abandoned.



The history-based pessimism (and the relevant debate) came to an end
by the triumph of atomism in the first decade of the twentieth
century. Due to the work of Albert Einstein and the French physicist
Jean Perrin on the atomic explanation of Brownian motion, one after
the other of major scientists who were initially sceptical about the
atomic conception of matter came to accept
 atomism.[4]
 The French philosopher Andre Lalande captured this point in
his 1913 (pp. 366-367) thus:



> 
> 
> M. Perrin, professor of physics at the Sorbonne, has described in
> *Les Atomes*, with his usual lucidity and vigour, the recent
> experiments (in which he has taken so considerable a part) which prove
> conclusively that the atoms are physical realities and not symbolical
> conceptions as people have for a long time been fond of calling them.
> By giving precise and concordant measures for their weights and
> dimensions, it is proved that bodies actually exist which, though
> invisible, are analogous at all points to those which we see and
> touch. An old philosophical question thus receives a positive
> solution.
> 
> 
> 



Be that as it may, what this brief account of the history of the
historical challenge to realism reveals are the two major lines of
defense of realism at play. Both lines of defense are based on the
presence of substantial continuity in theory-change in the history of
science. This continuity suggests that the disruption of the
scientific image of the world, as theories change, is less radical
than is assumed by the historical challenge to realism. But the two
lines of defense (the Poincare-Duhem and the Boltzmann one)
disagree over what is retained when theories change. The
Poincare-Duhem line of defense focuses on mathematical
equations (which express relations) and claims that only relations
among unobservable things are knowable, whereas the Boltzmann line of
defense focuses on whatever theoretical elements (including entities
like atoms) are retained while theories change; hence, it does not
limit scientific knowledge to the knowledge of relations only. Both
lines have resurfaced in the current debate.


## 2. Scientific Realism and the Pessimistic Induction


### 2.1 The 'Disastrous Meta-Induction'



Capitalizing on the work of Richard Boyd, the early Hilary Putnam took
scientific realism to involve three theses:


1. Theoretical terms refer to unobservable entities;
2. Theories are (approximately) true; and
3. There is referential continuity in theory change.



Putnam argued that the failure of the third thesis would lead to a
disastrous "meta-induction":



> 
> 
> *just as no term used in the science of more than fifty* (or
> whatever) *years ago referred, so it will turn out that no term
> used now* (except maybe observation terms, if there are such)
> *refers* (1978: 25) (emphasis in the original).
> 
> 
> 



An answer to this 'disastrous' history-fed argument was
the development of a causal theory of reference, which allows for
referential continuity in theory-change. This theory was first
suggested by Saul Kripke (1972) as an alternative to the then dominant
descriptive theories of reference of proper names and was extended by
Putnam (1973, 1975) to cover natural kind terms and theoretical terms.
According to the causal theory, the reference of a theoretical term
*t* is fixed during an introducing event in which an entity or
a physical magnitude is posited as the cause of various observable
phenomena. The term *t*, then, refers to the posited entity.
Though some kind of descriptions of the posited entity will be
associated with *t*, they do not play a role in reference
fixing. The referent has been fixed *existentially*: it is the
entity causally responsible for certain effects.



The causal theory of reference makes it possible that the same term
featuring in different theories refers to the same worldly entity. If,
for instance, the referent of the term 'electricity' is
fixed existentially, all different theories of electricity refer to,
and dispute over, the same 'existentially given'
magnitude, viz. *electricity*; better, the causal agent of
salient electrical effects. Hence, the causal theory makes available a
way to compare past and present theories and to claim that the
successor theory is more truthlike than its predecessors since it says
truer things of the same entities. It turns out, however, that the
causal theory faces a number of conceptual problems, most notable of
which is that it makes referential success inevitable insofar as the
phenomena which lead to the introduction of a new theoretical term do
have a cause (see Psillos 1999: chapter 11 for a discussion).
Philosophers of science have tried to put forward a causal-descriptive
theory of reference which makes referential continuity possible whilst
allowing room for causal descriptions in fixing the reference of a
theoretical
 term.[5]


### 2.2 The Principle of No Privilege



An analogous history-fed pessimistic argument can be based on the
so-called "principle of no privilege", which was advanced
by Mary Hesse in her 1976. According to this principle:



> 
> 
> our own scientific theories are held to be as much subject to radical
> conceptual change as past theories are seen to be. (1976: 266)
> 
> 
> 



This principle can be used for the derivation of the strong conclusion
that all theories are *false*. As Hesse put it:



> 
> 
> Every scientific system implies a conceptual classification of the
> world into an ontology of fundamental entities and properties--it
> is an attempt to answer the question "What is the world really
> made of?" But it is exactly these ontologies that are most
> subject to radical change throughout the history of science. Therefore
> in the spirit of the principle of no privilege, it seems that we must
> say either that all these ontologies are true, ie: we must give a
> realistic interpretation of all of them or we must say they are all
> false. But they cannot all be true in the same world, because they
> contain conflicting answers to the question "What is the world
> made of?" Therefore they must all be false. (1976: 266)
> 
> 
> 



This argument engages the history of theory-change in science in a
substantial way. As Hesse admitted, the Principle of No Privilege
arises "from accepting the induction from the history of
science" (1976: 271). Hesse's argument starts with the
historical premise that, as science grows over time, there has been a
recognizable pattern of change in the 'ontology of fundamental
entities and properties' posited by scientific theories.
Assuming, then, the Principle of No Privilege, it is argued that
current theories too will be subjected to a radical change in the
ontology of the entities and properties they posit. Hence, current
theories are as false as the past ones.



The problem with this kind of argument is that the historical premise
should be borne out by the actual history of theory-change in science.
It's not enough to say that scientific theories change over
time; these changes should be such that the newer theories are
incompatible with the past ones. Or, to use Hesse's idiom, it
should be shown that past and current scientific
'ontologies' are incompatible with each other. Showing
incompatibility between the claims made by current theory *T*
and a past theory *T*' requires a theory of reference of
theoretical terms which does *not* allow that terms featuring
in different theories can nonetheless refer to the same entity in the
world. Hence, it is question-begging to adopt a theory of reference
which makes it inevitable that there is radical-reference variance in
theory-change.



Referential stability, as noted already, makes possible the claim that
past and present ontologies are compatible, even if there have been
changes in what current theories say of the posited entities. The
"revolutionary induction from the history of science about
theory change" (Hesse 1976: 268) can be blocked by pointing to a
pattern of substantial continuity in theory change.


### 2.3 Getting Nearer to the Truth



Can a history-fed argument be used in *defence* of realism?
William Newton-Smith (1981) was perhaps the first in the recent debate
to answer positively this question. Scientific realism is committed to
the two following theses:


1. theories are true or false in virtue of how the world is, and
2. the point of the scientific enterprise is to discover explanatory
truths about the world.



According to Newton-Smith, (2) is under threat "if we reflect on
the fact that all physical theories in the past have had their heyday
and have eventually been rejected as false". And he added:



> 
> 
> Indeed, there is inductive support for a pessimistic induction: any
> theory will be discovered to be false within, say 200 years of being
> propounded. We may think of some of our current theories as being
> true. But modesty requires us to assume that they are not so. For what
> is so special about the present? We have good inductive grounds for
> concluding that current theories--even our most favourite
> ones--will come to be seen to be false. Indeed the evidence might
> even be held to support the conclusion that no theory that will ever
> be discovered by the human race is strictly speaking true. So how can
> it be rational to pursue that which we have evidence for thinking can
> never be reached? (1981: 14)
> 
> 
> 



The key answer to this question is that even if truth cannot be
reached, it is enough for the defense of realism to posit "an
interim goal for the scientific enterprise", viz., "the
goal of getting nearer the truth". If this is the goal, the
"sting" of the preceding induction "is
removed". Accepting PI "is compatible with maintaining
that current theories, while strictly speaking false, are getting
nearer the truth" (1981: 14).



But aren't all false theories equally false? The standard
realist answer is based on what Newton-Smith called "the animal
farm move" (1981: 184), viz., that though all theories are
false, some are truer than others. Hence, what was needed to be
defended was the thesis that if a theory \(T\_2\) has greater
verisimilitude than a theory \(T\_1\), \(T\_2\) is likely to have
greater observational success than \(T\_1\). The key argument was based
on the "undeniable fact" that newer theories have yielded
better predictions about the world than older ones (cf. Newton-Smith
1981: 196). But if the 'greater verisimilitude' thesis is
correct (that is, if theories "are increasing in truth-content
without increasing in falsity-content"), then the increase in
predictive power would be explained and rendered expectable. This
increase in predictive power "would be totally mystifying
(...) if it were not for the fact that theories are capturing
more and more truth about the world" (1981: 196).



The key point, then, is that the defense of realism against the
historical induction requires showing that there is, indeed, a
privilege that current theories enjoy over past ones, which is strong
enough to block transferring, on inductive grounds, features of past
theories to current ones. For most realists, the privilege current
theories enjoy over past ones is not that they are true while the past
theories are false. Rather, the privilege is that they are more
truthlike than past theories because they have had more predictive
power than past theories. The privilege is underpinned by an
explanatory argument: the increasing truthlikeness of current theories
*best explains* their increasing predictive and empirical
success.



But there is a way to see the historical challenge to realism which
makes it have as its target precisely to undercut the explanatory link
between empirical success and *truthlikeness*. This was brought
under sharp relief in the subsequent debates.


### 2.4 The Plethora of False Theories



The most famous history-based argument against realism, issued by
Larry Laudan (1981), was meant to show how the explanatory link
between success and truthlikeness is undermined by taking seriously
the history of science. It should be noted that Laudan's
argument has been subjected to several diverging interpretations,
which will be the focus of section 2.8. For the time being let's
stick to a particularly popular one, according to which Laudan argues
inductively from the falsity of past theories to the falsity of
current ones. This argument may be put thus:



(L)
The history of science is full of theories which had been
empirically successful for long periods of time and yet were shown to
be false about the deep-structure claims they had made about the
world. It is similarly full of theoretical terms featuring in
successful theories which do not refer. Therefore, by a simple (meta)
induction on scientific theories, our current successful theories are
likely to be false.


Laudan substantiated (L) by means of what he has called "the
historical gambit": the following list--which "could
be extended *ad nauseam*"--gives theories which were
once empirically successful and fruitful, yet just false.



Laudan's list of successful-yet-false theories


* the crystalline spheres of ancient and medieval astronomy
* the humoral theory of medicine
* the effluvial theory of static electricity
* catastrophist geology, with its commitment to a universal
(Noachian) deluge
* the phlogiston theory of chemistry
* the caloric theory of heat
* the vibratory theory of heat
* the vital force theory of physiology
* the theory of circular inertia
* theories of spontaneous generation
* the contact-action gravitational ether of Fatio and LeSage
* the optical ether
* the electromagnetic ether



This is a list of a dozen of cases, but Laudan boldly noted the famous
6 to 1 ratio:



> 
> 
> I daresay that for every highly successful theory in the past of
> science which we now believe to be a genuinely referring theory, one
> could find half a dozen once successful theories which we now regard
> as substantially non-referring. (1981: 35)
> 
> 
> 



If we are to take seriously this "plethora" of theories
that were both successful and false, it appears that (L) is meant to
be a genuinely *inductive* argument.



(I)
There has been a plethora of theories (*ratio 6 to 1*)
which were successful and yet not truthlike.



Therefore, it is highly probable that current theories will not be
truthlike (despite their success).




An argument such as (I) has obvious flaws. Two are the most important.
The first is that the basis for induction is hard to assess. This does
not just concern the 6:1 ratio, of which one may ask: *where does
it come from?* It also concerns the issue of how we individuate
and count theories as well as how we judge success and referential
failure. Unless we are clear on all these issues in advance of the
inductive argument, we cannot even start putting together the
inductive evidence for its conclusion (cf. Mizrahi 2013).



The second flaw of (I) is that the conclusion is *too* strong.
It is supposed to be that there is rational warrant for the judgment
that current theories are *not* truthlike. The flaw with this
kind of sweeping generalization is precisely that it totally
disregards the fresh strong evidence there is for current
theories--it renders current evidence totally irrelevant to the
issue of their probability of being true. Surely this is unwarranted.
Not only because it disregards potentially important differences in
the quality and quantity of evidence there is for current theories
(differences that would justify treating current theories as more
supported by available evidence than past theories were by the then
available evidence); but also because it makes a mockery of looking
for evidence for scientific theories! If I know that *X* is
more likely than *Y* and that this relation cannot change by
doing *Z*, there is no point in doing *Z*. 



The second flaw of (I) becomes (even more) apparent when one takes a
closer look at the successful-yet-false theories in Laudan's
list. Would anyone be willing to insist that, say, the humoral theory
of medicine, the vital force theory of physiology or the theory of
crystalline spheres are on a par with our current scientific theories
with the same domain of application? The difference between their
respective evidence is undoubtedly enormous. Nevertheless, it would
rather be mistaken to restrict our attention to those theories
comprising Laudan's *own* list. Indeed, subsequent
scholars have provided new lists of cases where admittedly false
theories had been used in the derivation of impressive empirical
predictions. Most notably, Timothy Lyons (2002: 70-72) and Peter
Vickers (2013: 191-194) suggest the following (partly overlapping)
lists:



Lyons's list


* Caloric Theory
* Phlogiston Theory
* Rankine's 19th Century Vortex Theory
* Newtonian Mechanics
* Fermat's Principle of Least Time
* Fresnel's Wave Theory of Light and of the Optical Ether
* Maxwell's Ether Theory
* Dalton's Atomic Theory
* Kekule's Theory of Benzene Molecule
* Mendeleev's Periodic Law
* Bohr's Theory of the Atom
* Dirac's Relativistic Wave Equation
* The Original (pre-inflationary) Big Bang Theory



Vickers's list


* Caloric Theory
* Phlogiston Theory
* Fresnel's theory of light and the luminiferous ether
* Rankine's vortex theory of thermodynamics
* Kekule's Theory of Benzene Molecule
* Dirac and the positron
* Teleomechanism and gill slits
* Reduction division in the formation of sex cells
* The Titius-Bode law
* Kepler's predictions concerning the rotation of the sun
* Kirchhoff's theory of diffraction
* Bohr's prediction of the spectral lines of ionized
helium
* Sommerfeld's prediction of the hydrogen fine structure
* Velikovsky and Venus
* Steady state cosmology
* The achromatic telescope
* The momentum of light
* S-matrix theory
* Variation of electron mass with velocity
* Taking the thermodynamic limit



These lists summarize much of the work done by historians of science
and historically informed philosophers of science. They are meant to
present cases of empirical successes that were (supposedly) brought
about by false theoretical hypotheses, hence offering a fresh source
of historical challenges to realism. At first sight, the cases
provided look substantially different from the majority of
Laudan's examples (viz. the successes, in at least some of them,
are more impressive). Yet, it remains to be seen whether they are more
troublesome for scientific realism.


### 2.5 The *Divide et Impera* Strategy



If we think of the pessimistic argument not as inductive but as a
*warrant-remover argument* and if we also think that the fate
of (past) theories should have a bearing on what we are warranted in
accepting now, we should think of its structure differently. It has
been argued by Psillos (1999: chapter 5) that we should think of the
pessimistic argument as a *kind* of reductio. Argument (L)
above aimed to "discredit the claim that there is an explanatory
connection between empirical success and truth-likeness" which
would warrant the realist view that current successful theories are
truthlike. If we view the historical challenge this way, viz., as a
potential warrant-remover argument, the past record of science does
play a role in it, since it is meant to offer this
warrant-remover.



Psillos's (1996) reconstruction of Laudan's argument was
as follows:



> 
> 
> Argument (P):
> 
> 
> 
> (A) Currently successful theories are truthlike.
> 
> 
> 
> (B) If currently successful theories are truthlike, then past theories
> are not.
> 
> 
> 
> (C) These characteristically false past theories were, nonetheless,
> empirically successful. (The 'historical gambit')
> 
> 
> 
> Hence, empirical success is not connected with truthlikeness and
> truthlikeness cannot explain success: the realist's potential
> warrant for (A) is defeated.
> 
> 
> 



Premise (B) of argument (P) is critical. It is meant to capture
radical discontinuity in theory-change, which was put thus (stated in
the material mode):



> 
> 
> Past theories are deemed not to have been truth-like because the
> entities they posited are no longer believed to exist and/or because
> the laws and mechanisms they postulated are not part of our current
> theoretical description of the world. (Psillos 1999: 97).
> 
> 
> 



In this setting, the 'historical gambit' (C) makes perfect
sense. Unless there are past successful theories which are
*warrantedly* deemed not to be truthlike, premise (B) cannot be
sustained and the warrant-removing reductio of (A) fails. If (C) can
be substantiated, success cannot be used to warrant the claim that
current theories are true. The realists' explanatory link
between truthlikeness and empirical success is undercut. (C) can be
substantiated only by examining past successful theories and their
fate. History of science is thereby essentially engaged.



The realist response has come to be known as the *divide et
impera* strategy to refute the pessimistic argument. The focus of
this strategy was on rebutting the claim that the truth of current
theories implies that past theories cannot be deemed truthlike. To
defend realism, realists needed to be selective in their commitments.
This selectivity was developed by Kitcher (1993) and (independently)
by Psillos (1994).



One way to be selective is to draw a distinction between *working
posits* of a theory (viz., those theoretical posits that occur
substantially in the explanatory schemata of the theory) and
*presuppositional posits* (putative entities that apparently
have to exist if the instances of the explanatory schemata of the
theory are to be true) (cf. Kitcher 1993: 149). Another way is to draw
a distinction between the theoretical claims that essentially or
ineliminably contribute to the generation of successes of a theory and
those claims that are 'idle' components that have had no
contribution to the theory's success (cf. Psillos 1994, 1996).
The underlying thought is that the empirical successes of a theory do
not indiscriminably support all theoretical claims of the theory, but
rather the empirical support is differentially distributed among the
various claims of the theory according to the contribution they make
to the generation of the successes. Generally, Kitcher (1993) and
Psillos (1996, 1999) have argued that there are ways to distinguish
between the 'good' and the 'bad'
*parts* of past abandoned theories and to show that the
'good' parts--those that enjoyed evidential support,
were not idle components and the like--were retained in
subsequent theories.



It is worth-noting that, methodologically, the *divide et
impera* strategy recommended that the historical challenge to
realism can only be met by looking at the actual successes of past
successful theories and by showing that those parts of past theories
(e.g., the caloric theory of heat or the optical ether theories) that
were fuelling theory successes were retained in subsequent theories
and those theoretical terms which were central in the relevant past
theories were referential. In fact, Vickers has recently made the
methodological suggestion that if one's *sole* aim is to
cope with a historical challenge, then it is sufficient that one shows
that the abandoned hypotheses were *not* essential for the
relevant theory's empirical success, without at the same time
taking side on which *are* the essential theoretical
hypotheses. As Vickers claims, in order to respond to a PI-style
challenge, "all the realist needs to do is show that the
specific assumptions identified by the antirealist do *not*
merit realist commitment. And she can do this without saying anything
about how to identify the posits which *do* merit realist
commitment" (2017: 3224). Besides, according to Vickers's
conception of the dialectic of the PI-debate, the onus of proof lies
with the antirealist: the antirealist has to reconstruct the
derivation of a prediction, identify the assumptions that merit
realist commitments and then show that at least one of them is not
truthlike by our current lights; and then all the realists need to
show is that the specific assumptions were inessential. In sum,
Vickers argues that "the project of responding to the historical
challenge" and "the project of explaining what realists
should commit to" have to be kept distinct (2017: 3222). 



At any rate, either employed in the identification of the trustworthy
theoretical parts or in the (mere) handling of a historical challenge,
the *divide et impera* move suggests that there has been enough
theoretical continuity in theory-change to warrant the realist claim
that science is 'on the right track.


### 2.6 Criticisms of *Divide et Impera*



The realist move from substantive continuity in theory-change to
truthlikeness has been challenged on grounds that there is no
entitlement to move from whatever preservation in theoretical
constituents there is in theory-change to these constituents'
being truthlike (Chang 2003: 910-12; Stanford 2006). Against
this point it has been argued that the realist strategy proceeds in
two steps (cf. Psillos 2009: 72). The first is to make the claim of
continuity (or convergence) plausible, viz., to show that there is
continuity in theory-change: substantive theoretical claims that
featured in past theories and played a key role in their successes
(especially novel predictions) have been incorporated in subsequent
theories and continue to play an important role in making them
empirically successful. But this first step does not establish that
the convergence is to the *truth*. For this claim to be made
plausible a second argument is needed, viz., that the emergence of
this evolving-but-convergent network of theoretical assertions is best
explained by the assumption that it is, by and large, truthlike. So
there is, after all, entitlement to move from convergence to
truthlikeness, insofar as truthlikeness is the best explanation of
this convergence.



Another critical point was that the *divide et impera* strategy
cannot offer independent support to realism since it is tailor-made to
suit realism: it is the fact that the very same present theory is used
*both* to identify which parts of past theories were
empirically successful *and* which parts were (approximately)
true that accounts for the realists' wrong impression that these
parts coincide (Stanford 2006). He says:



> 
> 
> With this strategy of analysis, an impressive retrospective
> convergence between our judgements of the sources of a past
> theory's success and the things it 'got right' about
> the world is virtually guaranteed: it is the very fact that some
> features of a past theory survive in our present account of nature
> that leads the realist *both* to regard them as true
> *and* to believe that they were the sources of the rejected
> theory's success or effectiveness. So the apparent convergence
> of truth and the sources of success in past theories is easily
> explained by the simple fact that both kinds of retrospective
> judgements have a common source in our present beliefs about nature.
> (2006: 166)
> 
> 
> 



It has been claimed by Psillos (2009) that the foregoing objection is
misguided. The problem is this. There are the theories scientists
currently endorse and there are the theories that had been endorsed in
the past. Some (but not all) of them were empirically successful
(perhaps for long periods of time). They were empirically successful
irrespective of the fact that, subsequently, they came to be replaced
by others. This replacement was a contingent matter that had to do
with the fact that the world did not fully co-operate with the then
extant theories: some of their predictions failed; or the theories
became overly ad hoc or complicated in their attempt to accommodate
anomalies, or what have you. The replacement of theories by others
does not cancel out the fact that the replaced theories were
empirically successful. Even if scientists had somehow failed to come
up with new theories, the old theories would not have ceased to be
successful. So success is one thing, replacement is another.



Hence, it is one thing to inquire into what features of some past
theories accounted for their success and quite another to ask whether
*these* features were such that they were retained in
subsequent theories of the same domain. These are two independent
issues and they can be dealt with (both conceptually and historically)
independently. One should start with some past theories
and--bracketing the question of their replacement--try to
identify, on independent grounds, the sources of their empirical
success; that is, to identify those theoretical constituents of the
theories that fuelled their successes. When a past theory has been, as
it were, anatomised, we can *then* ask the independent question
of whether there is any sense in which the sources of success of a
past theory that the anatomy has identified are present in our current
theories. It's not, then, the case that the current theory is
the common source for the identification of the successful parts of a
past theory *and* of its truthlike parts.



The transition from Newton's theory of gravity to
Einstein's illustrates this point. Einstein took it for granted
that Newton's theory of gravity (aided by perturbation theory)
could account for 531 arc-second per century of the perturbation of
Mercury's perihelion. Not only were the empirical successes of
Newton's theory identified independently of the successor
theory, but also some key theoretical components of Newton's
theory--the law of attraction and the claim that the
gravitational effects from the planets on each other were a
significant cause of the deviations from their predicted
orbits--were taken to be broadly correct and explanatory (of at
least part) of the successes. Einstein could clearly identify the
sources of successes of Newton's theory independently of his own
alternative theory and it is precisely for this reason that he
insisted that he had to recover Newton's law of attraction (a
key source of the Newtonian success) as a limiting case of his own
GTR. He could then show that his new theory could do both: it could
recover the (independently identified) sources of successes of
Newton's theory (in the form of the law of attraction)
*and* account for its failures by identifying further causal
factors (the curvature of space-time) that account for the
discrepancies between the predicted orbits of planets (by
Newton's theory of gravity) and the observed
 trajectories.[6]



Apart from Stanford's case against the *divide et impera*
move, the latter has become the target of criticism--among
others--by Timothy Lyons.
 [7] Lyons (2006) focuses his critique on Psillos's criterion
for the conditions under which a hypothesis indispensably contributes
to the derivation of novel predictions. In his (1999: 100) Psillos
says:



> 
> 
> Suppose that \(H\) together with another set of hypotheses \(H'\)
> (and some auxiliaries *A*) entail a
> prediction \(P\). \(H\) indispensably contributes to the
> generation of \(P\) if \(H'\) and *A* alone cannot
> yield \(P\) and no other available hypothesis \(H^\*\) which
> is consistent with \(H'\) and *A* can replace \(H\) without
> loss in the relevant derivation of \(P\). 
> 
> 
> 



Lyons interprets this passage--as well as Psillos's
subsequent claim that \(H^\*\) must satisfy some "natural epistemic
constraints", such as being "independently motivated, non
ad hoc, potentially explanatory etc." (ibid.)--as providing
the following criterion for the essential role of hypothesis \(H\) in the
derivation of prediction \(P\):



For \(H\) to be essential [for the derivation of \(P\)]:



(1)
It must be the case that \(H + H' + A\) leads to \(P\).
(2)
It must *not* be the case that \(H' + A\), alone, leads to
\(P\).
(3)
It must *not* be the case that any alternative, \(H^\*\), is
available 
 
(a)
that is consistent with \(H' + A\) and 
(b)
that when conjoined to \(H' + A\) leads to \(P\) and
(c)
that is non-*ad hoc* ([...] it does not use the data
predicted by \(P\) [...], is potentially explanatory, etc.) (Lyons
2006: 539).



Thus construed, Lyons criticizes Psillos' criterion for
essentiality, as being "superfluous, unmotivated, and therefore
inappropriate" (2006: 541). Briefly put, his point is that
condition 3 "unacceptably overshoots" the realist's
goal, since the absence of an alternative \(H^\*\) has "no bearing
whatsoever on whether \(H\) itself *contributed* to, was deployed
in, the derivation of a given prediction" (2006: 540). Besides,
Lyons states that condition 3 is so vague that it is "simply
inapplicable" (2006: 542). According to Mario Alai's
(2021) summary of Lyons's point, condition 3 doesn't
specify (*a*) *when* the alternative hypothesis \(H^\*\) must
or must not be available, (*b*) what 'potentially
explanatory etc.' means and (*c*) whether
\(H'\) and \(A\) must be essential too. In addition;
(*d*) it doesn't state whether \(H^\*\) is allowed to lead to
losses of other confirmed predictions and (*e*) whether \(H^\*\)
should be consistent with those elements of \(H'\)
and \(A\), which, though they are 'essential' for other
predictions, they are dispensable when it comes to the derivation of
the prediction under scrutiny. Based on these points, Lyons suggests
that even if realists might hold onto conditions 1 and 2 above,
condition 3 has to be abandoned, thereby isolating "the
deployment realist's fundamental insight", viz., that
credit should be attributed to those posits that
*actually*--as opposed to *essentially*--have
been deployed in the derivation of empirical predictions (2006,543).




In reply to Lyons, Peter Vickers (2017) and Alai (2021) have defended
the *divide et impera* move against the PI by suggesting the
following refinement of condition 3 (let's call it
3'):



(3')
\(H\) does not merit realist commitment whenever
\(H\) is doing work in the derivation solely in virtue of the fact that it
entails some other proposition \(H^\*\) which itself is sufficient, when
combined with the other assumptions in play, for the relevant
derivational step (Vickers, 2017: 3229).


According to Vickers, when realists are presented with an instance of
a (seemingly) success-inducing-yet-false hypothesis, all they need to
do is to show that the specific hypothesis does not satisfy the above
condition. It should be noted, however, that this, in essence, is the
strategy recommended by Psillos in his 1994, where he aimed to show,
using specific cases, that various assumptions such as that heat is a
material substance in the case of the caloric theory of heat, do not
merit realist commitment, because there are weaker assumptions that
fuel the derivation of successful predictions. 



Alai claims that substituting condition 3' for
condition 3 is an improvement of the *divide et impera* move,
for not only does condition 3' perform the task
that Psillos had in mind, but also escapes from Lyons'
criticisms (2021: 188). To begin with, condition
3' is said not to suffer from
the (alleged) vagueness of condition 3, for according to Alai:
(*a*) there is no question about *when* the alternative
\(H^\*\) is *available*; (*b*) there is no need to specify
what 'explanatory' means; and (*c*) it is not
required that \(H'\) and \(A\) are also essential. In
addition, (*d*) condition 3' allows that
\(H^\*\) may lead to losses of other confirmed predictions and (*e*),
since 3' excludes only hypotheses \(H^\*\) which are
entailed by \(H\), \(H^\*\) are ipso facto consistent with
\(H'\) and \(A\).



Now, it is rather evident that condition 3' is neither
superfluous nor unmotivated, since as Alai (2021, 188) stressed it is
motivated by a plausible epistemic principle associated with the
Occam's razor:



> 
> 
> in abductions we can assume only what is essential, i.e., the weakest
> hypothesis sufficient to explain a given effect; but if a hypotheses
> [sic], although deployed, was not essential in deriving [the novel
> prediction at hand], it is not essential in explaining its derivation
> either; therefore deployment realists need not (and must not) be
> committed to its truth. 
> 
> 
> 



In sum, *contra* Lyons, condition 3  is both
epistemologically motivated as well as indispensable for the proper
application of the *divide et impera* move. 



The 'Vickers-Alai' refinement of the *divide et
impera* move has not been uncontested. It has been criticized on
principled grounds, as well as for not being sufficient in dealing
with PI-style challenges. For instance, Dean Peters (2014) argues
*inter alia* that Vickers' criterion for essentiality
cannot account for the unificatory aspect of scientific theorizing,
whereas Florian Boge (2021) and Dana Tulodziecki (2021) have provided
new historical counterexamples--within the field of nuclear
physics and phychometry, and the 19th century miasma theory
of disease, respectively--that cannot be handled, or so it is
argued, by the 'Vickers-Alai' criterion. 



It should also be noted that, according to Vickers himself, the
employment of condition 3' in dealing with PI
seems to bring scientific realism dangerously close to structural
realism. As has already been said, Vickers's recipe for handling
a PI-style challenge is roughly the following: take the (false)
hypothesis \(H\) that, according to the anti-realist, is employed
in the derivation of a prediction \(P\), identify an
(uncontested) \(H^\*\) which is entailed by \(H\) and show
that \(H^\*\) is enough for the derivation of \(P\). This
recipe goes a long way in disarming Lyon's objection. And yet,
Vickers notes, an even weaker hypothesis \(H^{\*\*}\) is available, viz., that
for the prediction of P only the mathematical structure of \(H^\*\) is
required. But then, "only the very abstract
'structure' truly merits realist commitment, as structural
realists like to claim" (2017: 3227). If we take
'structure' to be identified with the Ramsey sentence of a
given theory (see the next section), then Vickers' concern is,
at least *prima facie*, a plausible one. For the Ramsey
sentence of a theory is obviously entailed by the latter and, as is
well known, any theory and its Ramsey sentence have exactly the same
observational consequences. Hence, it seems that the employment of
condition 3' forces realists to restrict their
commitment solely towards the Ramsey sentences of their favoured
theories. In reply, however, it should be stressed that though
Vickers's concern is *prima facie* warranted, it is far
from conclusive. In fact, after raising his concern, Vickers
doesn't further explore it, whereas Alai (2021: 211-212) has
argued that from the mere application of condition
3' "it doesn't follow that every
hypothesis is dispensable in favor of its Ramsey sentence".


### 2.7 Structural Realism



An instance of the *divide et impera* strategy is structural
realism. This view has been associated with John Worrall (1989), who
revived the relationist account of theory-change that emerged in the
beginning of the twentieth century. In opposition to scientific
realism, structural realism restricts the cognitive content of
scientific theories to their mathematical structure together with
their empirical consequences. But, in opposition to instrumentalism,
structural realism suggests that the mathematical structure of a
theory represents the structure of the world (real relations between
things). Against PI, structural realism contends that there is
continuity in theory-change, but this continuity is (again) at the
level of mathematical structure. Hence, the 'carried over'
mathematical structure of the theory correctly represents the
structure of the world and this best explains the predictive success
of a
 theory.[8]



Structural realism was independently developed in the 1970s by Grover
Maxwell (1970a, 1970b) in an attempt to show that the Ramsey-sentence
approach to theories need not lead to instrumentalism.
Ramsey-sentences go back to a seminal idea by Frank Ramsey (1929). To
get the Ramsey-sentence \(^{R}T\) of a (finitely axiomatisable) theory
*T* we conjoin the axioms of *T* in a single sentence,
replace all theoretical predicates with distinct variables \(u\_i\),
and bind these variables by placing an equal number of existential
quantifiers \(\exists u\_i\) in front of the resulting formula. Suppose
that the theory *T* is represented as *T*
(\(t\_1\),..., \(t\_n\); \(o\_1\),..., \(o\_m\)), where
*T* is a purely logical \(m+n\)-predicate. The Ramsey-sentence
\(^{R}T\) of *T* is:

 

\[\exists u\_1 \exists u\_2\ldots \exists u\_{n} T (u\_1,\ldots ,u\_{n}; o\_1,\ldots,o\_{m}).\]


The Ramsey-sentence \(^{R}T\) that replaces theory *T* has
exactly the same observational consequences as *T*; it can play
the same role as *T* in reasoning; it is truth-evaluable if
there are entities that satisfy it; but since it dispenses altogether
with theoretical vocabulary and refers to whatever entities satisfy it
only by means of quantifiers, it was taken to remove the issue of the
reference of theoretical terms/predicates. 'Structural
realism' was suggested to be the view that: i) scientific
theories issue in existential commitments to unobservable entities and
ii) all non-observational knowledge of unobservables is *structural
knowledge*, i.e., knowledge not of their first-order (or
intrinsic) properties, but rather of their higher-order (or
structural) properties. The key idea here was that a Ramsey-sentence
satisfies both conditions (i) and (ii). So we might say that, if true,
the Ramsey-sentence \(^{R}T\) gives us knowledge of the structure of
the world: there is a certain structure which satisfies the
Ramsey-sentence and the structure of the world (or of the relevant
worldly domain) is isomorphic to this structure.



Though initially Worrall's version of structural realism was
different from Maxwell's, being focused on--and motivated
by--*Poincare's* argument for structural
continuity in theory-change, in later work Worrall came to adopt the
Ramsey-sentence version of structural realism (see appendix IV of
Zahar 2001).



A key problem with Ramsey-sentence realism is that though a
Ramsey-sentence of a theory may be empirically inadequate, and hence
false, if it *is* empirically adequate (if, that is, the
structure of observable phenomena is embedded in one of its models),
then it is bound to be true. For, as Max Newman (1928) first noted in
relation to Russell's (1927) structuralism, given some
cardinality constraints, it is guaranteed that there is an
interpretation of the variables of \(^{R}T\) in the theory's
intended
 domain.[9]



More recently, David Papineau (2010) has argued that if we identify
the theory with its Ramsey-sentence, it can be argued that past
theories are approximately true if there are entities which satisfy,
or nearly satisfy, their Ramsey-sentences. The advantage of this move,
according to Papineau, is that the issue of referential failure is
bypassed when assessing theories for approximate truth, since the
Ramsey sentence replaces the theoretical terms with existentially
bound variables. But as Papineau (2010: 381) admits, the force of the
historical challenge to realism is not thereby thwarted. For it may
well be the case that the Ramsey-sentences of most past theories are
not satisfied (not even nearly
 so).[10]


### 2.8 Induction or Deduction?



In the more recent literature, there has been considerable debate as
to how exactly we should understand PI. There are those, like Anjan
Chakravartty who take it that PI is an Induction. He says:



> 
> 
> PI can ... be described as a two-step worry. First, there is an
> assertion to the effect that the history of science contains an
> impressive graveyard of theories that were previously believed [to be
> true], but subsequently judged to be false ... Second, there is
> an induction on the basis of this assertion, whose conclusion is that
> current theories are likely future occupants of the same graveyard.
> (2008: 152)
> 
> 
> 



Yet, it is plausible to think that *qua* an inductive argument,
history-based pessimism is bound to fail. The key point here is that
the sampling of theories which constitute the inductive evidence is
neither random nor otherwise representative of theories in
general.



It has been argued that, seen as an inductive argument, PI is
fallacious: it commits the base-rate fallacy (cf. Lewis 2001). If in
the past there have been many more false theories than true ones, (if,
in other words, truth has been rare), it cannot be concluded that
there is no connection between success and truth. Take *S* to
stand for Success and not-*S* to stand for failure.
Analogously, take *T* to stand for truth of theory *T*
and not-*T* for falsity of theory *T*. Assume also that
the probability that a theory is unsuccessful given that it is true is
zero \((\textrm{Prob}({\textrm{not-}S}\mid T)=0)\) and that the
probability that a theory is successful given that it is false is
0.05 \((\textrm{Prob}(S\mid {\textrm{not-}T})=0.05)\). Assume that is,
that there is a very high True Positives (successful but true) rate
and a small False Positives (successful but false theories) rate. We
may then ask the question: How likely is it that a theory is true,
given that it is successful? That is, what is the posterior
probability \(\textrm{Prob}(T\mid S)\)?



This answer is indeterminate if we don't take into account the
base-rate of truth, viz., the incidence rate of truth in the
population of theories. If the base rate is very low (let's
assume that only 1 in 50 theories have been true), then it is
*unlikely* that *T* is true given success.
\(\textrm{Prob}(T\mid S)\) would be around 0.3. But this does not imply
something about the connection between success and truth. It is still
the case that the false positives are low and that the true positives
high. The low probability is due to the fact that truth is rare (or
that falsity is much more frequent). For \(\textrm{Prob}(T\mid S)\) to be
high, it must be the case that \(\textrm{Prob}(T)\) is not too small.
But if \(\textrm{Prob}(T)\) is low, it can dominate over a high
likelihood of true positives and lead to a very low posterior
probability \(\textrm{Prob}(T\mid S)\). Similarly, the probability that a
theory is false given that it is successful (i.e.,
\(\textrm{Prob}({\textrm{not-}T}\mid S))\) may be high simply because
there are a lot more false theories than true ones. As Peter Lewis put
it:



> 
> 
> At a given time in the past, it may well be that false theories vastly
> outnumber true theories. In that case, even if only a small proportion
> of false theories are successful, and even if a large proportion of
> true theories are successful, the successful false theories may
> outnumber the successful true theories. So the fact that successful
> false theories outnumber successful true theories at some time does
> nothing to undermine the reliability of success as a test for truth at
> that time, let alone at other times (2001: 376-7).
> 
> 
> 



Seen in this light, PI does not discredit the reliability of success
as a test for truth of a theory; it merely points to the fact that
truth is scarce among past
 theories.[11]



Challenging the inductive credentials of PI has acquired a life of its
own. A standard objection (cf. Mizrahi 2013) is that theories are not
uniform enough to allow an inductive generalization of the form
"seen one, seen them all". That is, theories are diverse
enough over time, structure and content not to allow us to take a few
of them--not picked randomly--as representative of all and
to project the characteristics shared by those picked to all theories
in general. In particular, the list that Laudan produced is not a
random sample of theories. They are all before the twentieth century
and all have been chosen solely on the basis that they had had some
successes (irrespective of how robust these successes were). An
argument of the form:




*X* % of past successful theories are false



Therefore, *X* % of all successful theories are false




would be a weak inductive argument because



> 
> 
> it fails to provide grounds for projecting the property of the
> observed members of the reference class to unobserved members of the
> reference class. (Mizrahi 2013: 3219)
> 
> 
> 



Things would be different, if we had a random sampling of theories.
Mizrahi (2013: 3221-3222) collected 124 instances of
'theory' from various sources and picked at random 40 of
them. These 40 were then divided into three groups: accepted theories,
abandoned theories and debated theories. Of those 40 theories, 15%
were abandoned and 12% debated. Mizrahi then notes that these randomly
selected data cannot justify an inductively drawn conclusion that most
successful theories are false. On the contrary, an optimistic
induction would be more warranted:




72% of sampled theories are accepted theories (i.e., considered
true).



Therefore, 72% of all theories are accepted theories (i.e., considered
true).




Mizrahi has come back to the issue of random sampling and has
attempted to show that the empirical evidence is against PI:



> 
> 
> If the history of science were a graveyard of dead theories and
> abandoned posits, then random samples of scientific theories and
> theoretical posits would contain significantly more dead theories and
> abandoned posits than live theories and accepted posits.
> 
> 
> 
> It is not the case that random samples of scientific theories and
> theoretical posits contain significantly more dead theories and
> abandoned posits than live theories and accepted posits.
> 
> 
> 
> Therefore, It is not the case that the history of science is a
> graveyard of dead theories and abandoned posits. (2016: 267)
> 
> 
> 



A similar argument has been defended by Park (2011). We may call it,
the explosion argument: Most key theoretical terms of successful
theories of the twentieth century refer "in the light of current
theories". But then, "most central terms of successful
past theories refer", the reason being that there are far more
twentieth century theories than theories in total. This is because
"the body of scientific knowledge exploded in the twentieth
century with far more human and technological resources" (2011:
79).



Let's call this broad way to challenge the inductive credentials
of the pessimistic argument 'the Privilege-for-current-theories
strategy'. This has been adopted by Michael Devitt (2007) too,
though restricted to entities. Devitt, who takes realism to be a
position concerning the existence of unobservables, noted that the
right question to ask is this: 'What is the "success
ratio" of past theories?', where the "success
ratio" is "the ratio of the determinately existents to the
determinately nonexistents + indeterminates". Asserting a
privilege for current science, he claims that "we are now
*much better* at finding out about unobservables".
According to him, then, it is "fairly indubitable" that
the historical record shows "improvement over time in our
success ratio for unobservables'.



In a similar fashion but focusing on current theories, Doppelt (2007)
claims that realists should confine their commitment to the
approximate truth of current best theories, where best theories are
those that are both most successful and well established. The
asymmetry between current best theories and past ones is such that the
success of current theories is of a different *kind* than the
success of past theories. The difference, Doppelt assumes, is so big
that the success of current theories can only be explained by assuming
that they are approximately true, whereas the explanation of the
success of past theories does not require this commitment.



If this is right, there is sufficient qualitative distance between
past theories and current best ones to block



> 
> 
> any pessimistic induction from the successful-but-false superseded
> theories to the likelihood that our most successful and
> well-established current theories are also probably false. (Doppelt
> 2007: 110).
> 
> 
> 



The key difference, Doppelt argues, is that



> 
> 
> our best current theories enjoy a singular degree of empirical
> confirmation impossible for their predecessors, given their ignorance
> of so many kinds of phenomena and dimensions of nature discovered by
> our best current theories.
> 
> 
> 



This singular degree of empirical confirmation amounts to raising the
standards of empirical success to a level unreachable by past theories
(cf. 2007: 112).



The advocate of PI can argue that past 'best theories'
also raised and met the standards of empirical success, which
inductively supports the conclusion that current best theories will be
superseded by others which will meet even higher standards of success.
Doppelt's reply is that this new version of PI "should not
be given a free pass as though it were on a par with the original
pessimistic induction" the reason being that "in the
history of the sciences, there is greater continuity in standards of
empirical success than in the theories taken to realize them".
Hence, the standards of empirical success change slower than theories.
Hence, it is not very likely that current standards of empirical
success will change any time soon.



It has been argued, however, that Doppelt cannot explain the novel
predictive success of past theories without arguing that they had
truthlike constituents (cf. Alai 2017). Besides, as Alai puts it,
"current best theories explain the (empirical) success of
discarded ones only to the extent that they show that the latter were
partly true" (2017: 3282).



The 'Privilege-for-current-theories strategy' has been
supported by Ludwig Fahrbach (2011). The key point of this strategy is
that the history of science does not offer a representative sample of
the totality of theories that should be used to feed the historical
pessimism of PI. In order to substantiate this, Fahrbach suggested,
based on extensive bibliometric data, that over the last three
centuries the number of papers published by scientists as well as the
number of scientists themselves have grown *exponentially*,
with a doubling rate of 15-20 years. Hence, he claims, the past
theories that feed the historical premise of PI were produced during
the time of the first 5% of all scientific work ever done by
scientists. As such the sample is totally unrepresentative of theories
in total; and hence the pessimistic conclusion, viz., that current
theories are likely to be false and abandoned in due course, is
inductively unwarranted. Moreover, Fahrbach argues, the vast majority
of theories enunciated in the last 50-80 years, (which
constitute the vast majority of scientific work ever produced) are
still with us. Hence, as he puts it,



> 
> 
> (t)he anti-realist will have a hard time finding even one or two
> convincing examples of similarly successful theories that were
> accepted in the last 50-80 years for some time, but later
> abandoned. (2011: 152)
> 
> 
> 



Since there have been practically no changes "among our best
(i.e., most successful) theories", Fahrbach suggests



> 
> 
> an optimistic meta-induction to the effect that they will remain
> stable in the future, i.e., all their empirical consequences which
> scientists will ever have occasion to compare with results from
> observation at any time in the future are true. (2011: 153)
> 
> 
> 



The conclusion is that the PI is unsound: "its conclusion that
many of our current best scientific theories will fail empirically in
the future cannot be drawn" (2011: 153).



A key assumption of the foregoing argument is that there is a strong
connection between the amount of scientific work (as measured by the
number of journal articles) and the degree of success of the best
scientific theories. But this can be contested on the grounds that
it's a lot easier to publish currently than it was in the
seventeenth century and that current research is more tightly
connected to the defense of a single theoretical paradigm than before.
This might well be a sign of maturity of current science but, as it
stands, it does not show that the present theoretical paradigm is not
subject to radical change. Florian Muller (2015) put the point in
terms of decreasing marginal revenues. The correlation between
increased scientific work and scientific progress, which is assumed by
Fahrbach may not be strong enough:



> 
> 
> It seems more plausible to expect decreasing marginal revenues of
> scientific work since it usually takes much less time to establish
> very basic results than to make progress in a very advanced state of
> science. (Muller 2015: 404)
> 
> 
> 



The 'Privilege-for-current-theories strategy' can be
further challenged on the grounds that it requires some
"fundamental difference between the theories we currently
accept, and the once successful theories we have since rejected"
(Wray 2013: 4325). As Brad Wray (2013) has argued Fahrbach's
strategy is doomed to fail because the argument from exponential
growth could be repeated at former periods too, thereby undermining
itself. Imagine that we are back in 1950 and we look at the period
between 1890 and 1950. We could then argue, along Farhbach's
lines, that the pre-1890 theories (which were false and abandoned)
were an unrepresentative sample of all theories and that the recent
theories (1890-1950) are by far the most theories until 1950 and
that, since most of them have not been abandoned (by 1950), they are
likely to remain impervious to theory-change. Or imagine that we are
further back in 1890 and look at the theories of the period
1830-1890. We could run the same argument about those theories,
viz, that they are likely to survive theory change. But if we look at
the historical *pattern*, they did not survive; nor did the
theories between 1890-1950. By the same token, we should not
expect current theories to survive theory-change.



Is there room for defending an epistemic privilege for current
science? Two points are worth making. The first is that it's
hard to defend some kind of epistemic privilege of current science if
the realist argument against PI stays only at a level of statistics
(even assuming that there can be statistics over theories). If there
is an epistemic privilege of current science in relation to past
science, it is not a matter of quantity but of *quality*. The
issue is not specifying how likely it is that an arbitrary current
theory *T* be true, given the evidence of the past record of
science. The issue, instead, is how a *specific* scientific
theory--a real theory that describes and explains certain
well-founded worldly phenomena--is supported by the evidence
there is for it. If we look at the matter from this perspective, we
should look at case-histories and not at the history of science at
large. The evidence there is for specific theory *T* (e.g., the
Darwinian synthesis or GTR etc.) need not be affected by past failures
in the theoretical understanding of the world in general. The reason
is that there is local epistemic privilege, that is, privilege over
past relevant theories concerning first-order evidence and specific
methods.



The second point is this. Wray's argument against Fahrbach is,
in effect, that there can be a temporal meta-(meta-)induction which
undermines at each time *t* (or period *Dt*) the
privilege that scientific theories at *t* or *Dt* are
supposed to have. So Wray's point is this: at each time
\(t\_{i}\) (or period \(Dt\_{i}\)), scientists claim that their theories
are not subject to radical change at subsequent times; but if we look
at the pattern of theory change over time, the history of science
shows that there have been subsequent times \(t\_{i}+1\) (or periods
\({Dt}\_{i}+1\)) such that the theories accepted at \(t\_{i}\) were
considered false and abandoned. Hence, he takes it that at no time
\(t\_{i}\) are scientists justified in accepting their theories as not
being subject to radical change in the future. But this kind of
argument is open to the following criticism. It assumes, as it were,
unit-homogeneity, viz., that science at all times \(t\_{i}\) (and all
periods \({Dt}\_{i}\)) is the same when it comes to how far it is from
the truth. Only on *this* assumption can it be argued that at
no time can scientists claim that their theories are not subject to
radical change. For if there are senses in which subsequent theories
are closer to the truth than their predecessors, it is not equally
likely that they will be overturned as their predecessors were.



The point, then, is that though at each time \(t\_{i}\) (or period
\({Dt}\_{i}\)) scientists might well claim that their theories are not
subject to radical change at subsequent times, they are not equally
*justified* in making this claim! There might well be times
\(t\_{i}\) (or periods \({Dt}\_{i}\)) in which scientists are more
justified in making the claims that their theories are not subject to
radical change at subsequent times simply because they have reasons to
believe that their theories are truer than their predecessors. To give
an example: if Wray's argument is right then Einstein's
GTR is as likely to be overthrown at future time \(t\_{2100}\) as was
Aristotle's crystalline spheres theory in past time
\(t\_{-300}\). But this is odd. It totally ignores the fact that all
available evidence renders GTR closer to the truth than the simply
false Aristotelian theory. In other words, that GTR has substantial
truth-content makes it less likely to be radically revised in the
future.



An analogous point was made by Park (2016). He defined what he called
*Proportional Pessimism* as the view that "as theories
are discarded, the inductive rationale for concluding that the next
theories will be discarded grows stronger" (2016: 835). This
view entails that the more theories have been discarded before
*T* is discarded, the more justified we are in thinking that
*T* is likely to be discarded. However, it is also the case
that based on their greater success, we are more justified to take
newer theories to be more likely to be truthlike than older ones. We
then reach a paradoxical situation: we are justified to take newer
theories to be both more probable than older ones and more likely to
be abandoned than older ones.



If an inductive rendering of historical pessimism fails, would a
deductive rendering fare better? Could PI be considered at least as a
*valid deductive argument*? Wray (2015: 65) interprets the
original argument by Laudan as being deductive. And he notes



> 
> 
> as far as Laudan is concerned, a single successful theory that is
> false would falsify the realist claim that (all) successful theories
> are true; and a single successful theory that refers to a non-existent
> type of entity would falsify the realist claim that (all) successful
> theories have genuinely referring theoretical terms.
> 
> 
> 



But if this is the intent of the argument, history plays *no
role* in it. All that is needed is a single counterexample, past
or present. This, it should be noted, is an endemic problem with all
attempts to render PI as a deductive argument. Muller, for
instance, notes that the fundamental problem raised by PI is
"simply that successful theories can be false". He
adds:



> 
> 
> Even just one counterexample (as long as it is not explained away)
> undermines the claim that truth is the best explanation for the
> success of theories as it calls into question the explanatory
> connection in general. (2015: 399)
> 
> 
> 



Thus put, the history of past failures plays no role in PI. Any
counterexample, even one concerning a current theory, will do.



How is it best to understand the realist theses that the history of
science is supposed to undermine? Mizrahi (2013: 3224) notes that the
realist claim is not meant to be a universal statement. As he puts
it:



> 
> 
> Success may be a reliable indicator of (approximate) truth, but this
> is compatible with some instances of successful theories that turn out
> not to be approximately true. In other words, that a theory is
> successful is a reason to believe that it is approximately true, but
> it is not a conclusive proof that the theory is approximately
> true.
> 
> 
> 



The relation between success and (approximate) truth, in this sense,
is more like the relation between flying and being a bird: flying
characterizes birds even if kiwis do not fly. If this is so, then
there is need for more than one counter-example for the realist thesis
to be undermined.



A recent attempt to render PI as a deductive argument is by Timothy
Lyons. He (2016b) takes realism to issue in the following
*meta-hypothesis*: "our successful scientific theories
are (approximately) true". He then reconstructs PI thus:



(D)

1.
If (a) the realist meta-hypothesis were true, then (b) we would
have no successful theories that cannot be approximately true. (If we
did, each would be a "miracle," which no one of us
accepts.)
2.
However, (not-b) we do have successful theories that cannot be
approximately true: the list (of
"miracles").
3.
Therefore, (not-a) the realist meta-hypothesis is false. (And
the no-miracles argument put forward to justify that meta-hypothesis
is unacceptable.)


This is supposed to be a deductive argument against the 'meta
hypothesis'. But in his argument the history of science plays no
role. All that is needed for the argument above to be sound is a
*single instance* of a successful theory that is not true. A
single non-white swan is enough to falsify the hypothesis 'All
swans are white'--there is no point in arguing here: the
more, the merrier! In a similar fashion, it doesn't add much to
argument (D) to claim



> 
> 
> the quest to empirically increase the quantity of instances (...)
> is rather to secure the soundness of the *modus tollens*, to
> secure the truth of the pivotal second premise, the claim that there
> are counterinstances to the realist meta-hypothesis. (Lyons 2016b:
> 566)
> 
> 
> 



In any case, a critical question is: can some
false-but-rigorously-empirically-successful theories justifiably be
deemed truthlike from the point of view of successor theories? This
question is hard to answer without looking at actual cases in the
history of science. The general point, made by Vickers (2017) is that
it is not enough for the challenger of realism to identify some
components of past theories which were contributing to their successes
such that they were not retained in subsequent theories. The
challenger of realism should show that false components "merit
realist commitment". If they do not, " (...) that is
enough to answer the historical challenge".



More generally, the search for a generic form of the pessimistic
*X*-duction (In-duction or De-duction) has yielded the
following problem: If the argument is inductive, it is at best weak.
If the argument is deductive, even if it is taken to be sound, it
makes the role of the history of science
 irrelevant.[12]


### 2.9 A New Induction



Stanford (2006) has aimed to replace PI with what he calls the
'new induction' on the history of science, according to
which past historical evidence of transient underdetermination of
theories by evidence makes it likely that current theories will be
supplanted by hitherto unknown (unconceived) ones, which nonetheless,
are such that when they are formulated, they will be at least as well
confirmed by the evidence as the current ones. But the new induction
is effective, if at all, only in tandem with PI. For if there is
continuity in our scientific image of the world, the hitherto
unconceived theories that will replace the current ones won't be
the radical rivals they are portrayed to
 be.[13]



When it comes to the realist commitment to theories, the proper
philosophical task is to ignore neither the first order scientific
evidence that there is for a given theory nor the lessons that can be
learned from the history of science. Rather, the task is to balance
the first-order and the second order of evidence. The *first-order
evidence* is typically associated with whatever scientists take
into account when they form an epistemic attitude towards a theory. It
can be broadly understood to include some of the theoretical virtues
of the theory at hand--of the kind that typically go into
plausibility judgments associated with assignment of prior probability
to theories. The *second-order evidence* comes from the past
record of scientific theories and/or from meta-theoretical
(philosophical) considerations that have to do with the reliability of
scientific methodology. It concerns not particular scientific
theories, but science as a whole. This second-order evidence feeds
claims such as those that motivate PI or the New Induction. Actually,
this second-order evidence is multi-faceted--it is negative
(showing limitations and shortcomings) as well as positive (showing
how learning from experience can be improved).