## 1. Introduction: Epistemology of Experiment



Epistemology of experiment is a branch of philosophy of science
focusing on the diverse roles that experiment plays in science, its
various connections to theory, to the understanding and functions of
experimental apparatus, and to the structure and culture of the
scientific community in the laboratory setting. The epistemological
analysis of experiments ranges from highly abstract philosophical
arguments with only indirect connection to actual practice, to
analysis immersed in reflective case studies. For a long time
experiments in physics have been the leading edge of experimental
science, pioneering experimental techniques, methods and innovative
settings. This is why much of epistemology of experiment has focused
on physics.



The 17th century witnessed the first philosophical reflections on the
nature of experimentation. This should not be surprising given that
experiment was emerging as a central scientific tool at the time. The
aim of these reflections was to uncover why nature reveals its hidden
aspects to us when we force experimental methods upon it.



Some natural philosophers believed that scientific knowledge was
little more than the proper application of observational and
experimental techniques on natural phenomena. Francis Bacon went so
far as to claim that it was possible to perform what he called a
crucial experiment (experimentum crucis), an ideal experiment of sorts
that can determine alone which of two rival hypotheses is correct. And
even some of the giants of modern science such as Newton subscribed to
the view that scientific theories are directly induced from
experimental results and observations without the help of untested
hypotheses. It is little wonder, then, that many natural philosophers
thought that experimental techniques and their proper application
should be a primary object of philosophical study of science.



Yet not everybody agreed. Hobbes, for instance pointed out that human
reason preceded experimental techniques and their application. He
thought that human reasoning reveals to us the natural law, and
criticized Boyle's optimism regarding experimental
method's ability to reveal it (Shapin and Schaffer 1984).
Doesn't human reason guide experimenter's actions, in the
way it leads us to choose data and samples, and the way it allows us
to interpret them, after all? If so, we should focus on the
philosophical study of reason and theoretical scientific reasoning
rather than on the study of experimental techniques and their
applications.



This vigorous early debate in many ways anticipated the main points of
disagreement in debates to come. Yet the philosophical interest in
experimentation almost completely lost its steam at the end of the
19th century and did not recover until fairly late in the 20th
century.



During that period philosophers turned much of their attention to the
study of the logical structure of scientific theories and its
connection to evidence. The tenets of logical positivism influenced
this area of investigation -- as well as philosophy more
generally -- at the time. One of these tenets stated that
observational and theoretical propositions in science are separable.
My readings of the gradation on the scale of a mercury thermometer can
be separated from rather complicated theoretical statements concerning
heat transfer and the theoretical concept of temperature.



In fact, not only can one separate theory and observation, but the
former is considered justified only in light of its correspondence
with the latter. The theory of heat transfer is confirmed by
propositions originating in the kind of readings I perform on my
mercury thermometer. Thus, observational propositions are simply a
result of an experiment or a set of observations a scientist performs
in order to confirm or refute a theory.



Thomas Kuhn and Paul Feyerabend vigorously criticized this view. They
argued that observations and experimental results are already part of
a theoretical framework and thus cannot confirm a theory
independently. Nor there is a theory-neutral language for capturing
observations. Even a simple reading of a mercury thermometer
inevitably depends on a theoretically-charged concept of temperature.
In short, the evidence is always theory-laden.



Yet neither the proponents of logical positivism nor their critics
ever attempted to explain the nature of experimentation that produces
all-important observational statements. And the reason for this was
very simple: they didn't think that there was anything
interesting to explain. Their views on the relationship between theory
and evidence were diametrically opposed, but they all found only the
final product of experimentation, namely observational statements,
philosophically interesting. As a result, the experimental process
itself was set aside in their philosophical study of science. This has
gradually changed only with the advent of New Experimentalism, with
Ian Hacking's work at its forefront.


## 2. Experimental Results


### 2.1 Learning From Experiment


#### 2.1.1 Representing and Intervening



It has been more than three decades since Ian Hacking asked,
"Do we see through a microscope?" (Hacking 1981).
Hacking's question really asked how do we come to believe in an
experimental result obtained with a complex experimental apparatus?
How do we distinguish between a valid
 result[2]
 and an artifact created by that apparatus? If experiment is to play
all of the important roles in science mentioned above and to provide
the evidential basis for scientific knowledge, then we must have good
reasons to believe in those results. Hacking provided an extended
answer in the second half of *Representing and Intervening*
(1983). He pointed out that even though an experimental apparatus is
laden with, at the very least, the theory of the apparatus,
observations remain robust despite changes in the theory of the
apparatus or in the theory of the phenomenon. His illustration was the
sustained belief in microscope images despite the major change in the
theory of the microscope when Abbe pointed out the importance of
diffraction in its operation. One reason Hacking gave for this is that
in making such observations the experimenters intervened--they
manipulated the object under observation. Thus, in looking at a cell
through a microscope, one might inject fluid into the cell or stain
the specimen. One expects the cell to change shape or color when this
is done. Observing the predicted effect strengthens our belief in both
the proper operation of the microscope and in the observation. This is
true in general. Observing the predicted effect of an intervention
strengthens our belief in both the proper operation of the
experimental apparatus and in the observations made with it.



Hacking also discussed the strengthening of one's belief in an
observation by independent confirmation. The fact that the same
pattern of dots--dense bodies in cells--is seen with
"different" microscopes, (e.g. ordinary, polarizing,
phase-contrast, fluorescence, interference, electron, acoustic etc.)
argues for the validity of the observation. One might question whether
"different" is a theory-laden term. After all, it is our
theory of light and of the microscope that allows us to consider these
microscopes as different from each other. Nevertheless, the argument
holds. Hacking correctly argues that it would be a preposterous
coincidence if the same pattern of dots were produced in two totally
different kinds of physical systems. Different apparatuses have
different backgrounds and systematic errors, making the coincidence,
if it is an artifact, most unlikely. If it is a correct result, and
the instruments are working properly, the coincidence of results is
understandable.


#### 2.1.2 Experimental Strategies



Hacking's answer is correct as far as it goes. It is, however,
incomplete. What happens when one can perform the experiment with only
one type of apparatus, such as an electron microscope or a radio
telescope, or when intervention is either impossible or extremely
difficult? Other strategies are needed to validate the
 observation.[3]
 These may include:


1. Experimental checks and calibration, in which the experimental
apparatus reproduces known phenomena. For example, if we wish to argue
that the spectrum of a substance obtained with a new type of
spectrometer is correct, we might check that this new spectrometer
could reproduce the known Balmer series in hydrogen. If we correctly
observe the Balmer Series then we strengthen our belief that the
spectrometer is working properly. This also strengthens our belief in
the results obtained with that spectrometer. If the check fails then
we have good reason to question the results obtained with that
apparatus.
2. Reproducing artifacts that are known in advance to be present. An
example of this comes from experiments to measure the infrared spectra
of organic molecules (Randall et al. 1949). It was not always possible
to prepare a pure sample of such material. Sometimes the experimenters
had to place the substance in an oil paste or in solution. In such
cases, one expects to observe the spectrum of the oil or the solvent,
superimposed on that of the substance. One can then compare the
composite spectrum with the known spectrum of the oil or the solvent.
Observation then of this artifact gives confidence in other
measurements made with the spectrometer.
3. Elimination of plausible sources of error and alternative
explanations of the result (the Sherlock Holmes
 strategy).[4]
 Thus, when scientists claimed to have observed electric discharges in
the rings of Saturn, they argued for their result by showing that it
could not have been caused by defects in the telemetry, interaction
with the environment of Saturn, lightning, or dust. The only remaining
explanation of their result was that it was due to electric discharges
in the rings--there was no other plausible explanation of the
observation. (In addition, the same result was observed by both
Voyager 1 and Voyager 2. This provided independent confirmation.
Often, several epistemological strategies are used in the same
experiment.)
4. Using the results themselves to argue for their validity. Consider
the problem of Galileo's telescopic observations of the moons of
Jupiter. Although one might very well believe that his primitive,
early telescope might have produced spurious spots of light, it is
extremely implausible that the telescope would create images that they
would appear to be a eclipses and other phenomena consistent with the
motions of a small planetary system. It would have been even more
implausible to believe that the created spots would satisfy
Kepler's Third Law (\(\bfrac{R^3}{T^2} = \) constant). A similar
argument was used by Robert Millikan to support his observation of the
quantization of electric charge and his measurement of the charge of
the electron. Millikan remarked, "The total number of changes
which we have observed would be between one and two thousand, and
*in not one single instance has there been any change which did not
represent the advent upon the drop of one definite invariable quantity
of electricity or a very small multiple of that quantity*"
(Millikan 1911, p. 360). In both of these cases one is arguing that
there was no plausible malfunction of the apparatus, or background,
that would explain the observations.
5. Using an independently well-corroborated theory of the phenomena
to explain the results. This was illustrated in the discovery of the
\(\ce{W^{\pm}}\), the charged intermediate vector boson required by
the Weinberg-Salam unified theory of electroweak interactions.
Although these experiments used very complex apparatuses and used
other epistemological strategies (for details see Franklin 1986, pp.
170-72). I believe that the agreement of the observations with
the theoretical predictions of the particle properties helped to
validate the experimental results. In this case the particle
candidates were observed in events that contained an electron with
high transverse momentum and in which there were no particle jets,
just as predicted by the theory. In addition, the measured particle
mass of \(81\pm 5\) GeV/c2 and \(80^{+10}\_{-6}\)
GeV/c2, found in the two experiments (note the independent
confirmation also), was in good agreement with the theoretical
prediction of \(82\pm 2.4\) GeV/c2. It was very improbable
that any background effect, which might mimic the presence of the
particle, would be in agreement with theory.
6. Using an apparatus based on a well-corroborated theory. In this
case the support for the theory inspires confidence in the apparatus
based on that theory. This is the case with the electron microscope
and the radio telescope, whose operations are based on a
well-supported theories, although other strategies are also used to
validate the observations made with these instruments.
7. Using statistical arguments. An interesting example of this arose
in the 1960s when the search for new particles and resonances occupied
a substantial fraction of the time and effort of those physicists
working in experimental high-energy physics. The usual technique was
to plot the number of events observed as a function of the invariant
mass of the final-state particles and to look for bumps above a smooth
background. The usual informal criterion for the presence of a new
particle was that it resulted in a three standard-deviation effect
above the background, a result that had a probability of 0.27% of
occurring in a single bin. This criterion was later changed to four
standard deviations, which had a probability of 0.0064% when it was
pointed out that the number of graphs plotted each year by high-energy
physicists made it rather probable, on statistical grounds, that a
three standard-deviation effect would be observed.



These strategies along with Hacking's intervention and
independent confirmation constitute an epistemology of experiment.
They provide us with good reasons for belief in experimental results,
They do not, however, guarantee that the results are correct. There
are many experiments in which these strategies are applied, but whose
results are later shown to be incorrect (examples will be presented
below). Experiment is fallible. Neither are these strategies exclusive
or exhaustive. No single one of them, or fixed combination of them,
guarantees the validity of an experimental result. Physicists use as
many of the strategies as they can conveniently apply in any given
experiment.


#### 2.1.3 Complexity of Experimental Practice



In *How Experiments End* (1987), Peter Galison extended the
discussion of experiment to more complex situations. In his histories
of the measurements of the gyromagnetic ratio of the electron, the
discovery of the muon, and the discovery of weak neutral currents, he
considered a series of experiments measuring a single quantity, a set
of different experiments culminating in a discovery, and two high-
energy physics experiments performed by large groups with complex
experimental apparatus.



Galison's view is that experiments end when the experimenters
believe that they have a result that will stand up in court--a
result that I believe includes the use of the epistemological
strategies discussed earlier. Thus, David Cline, one of the weak
neutral-current experimenters remarked, "At present I
don't see how to make these effects [the weak neutral current
event candidates] go away" (Galison, 1987, p. 235).



Galison emphasizes that, within a large experimental group, different
members of the group may find different pieces of evidence most
convincing. Thus, in the Gargamelle weak neutral current experiment,
several group members found the single photograph of a
neutrino-electron scattering event particularly important, whereas for
others the difference in spatial distribution between the observed
neutral current candidates and the neutron background was decisive.
Galison attributes this, in large part, to differences in experimental
traditions, in which scientists develop skill in using certain types
of instruments or apparatus. In particle physics, for example, there
is the tradition of visual detectors, such as the cloud chamber or the
bubble chamber, in contrast to the electronic tradition of Geiger and
scintillation counters and spark chambers. Scientists within the
visual tradition tend to prefer "golden events" that
clearly demonstrate the phenomenon in question, whereas those in the
electronic tradition tend to find statistical arguments more
persuasive and important than individual events. (For further
discussion of this issue see Galison 1997).



Galison points out that major changes in theory and in experimental
practice and instruments do not necessarily occur at the same time.
This persistence of experimental results provides continuity across
these conceptual changes. Thus, the experiments on the gyromagnetic
ratio spanned classical electromagnetism, Bohr's old quantum
theory, and the new quantum mechanics of Heisenberg and Schrodinger.
Robert Ackermann has offered a similar view in his discussion of
scientific instruments.



> 
> The advantages of a scientific instrument are that it cannot change
> theories. Instruments embody theories, to be sure, or we
> wouldn't have any grasp of the significance of their
> operation....Instruments create an invariant relationship between
> their operations and the world, at least when we abstract from the
> expertise involved in their correct use. When our theories change, we
> may conceive of the significance of the instrument and the world with
> which it is interacting differently, and the datum of an instrument
> may change in significance, but the datum can nonetheless stay the
> same, and will typically be expected to do so. An instrument reads 2
> when exposed to some phenomenon. After a change in
>  theory,[5]
>  it will continue to show the same reading, even though we may take
> the reading to be no longer important, or to tell us something other
> than what we thought originally (Ackermann 1985, p. 33).
> 



Galison also discusses other aspects of the interaction between
experiment and theory. Theory may influence what is considered to be a
real effect, demanding explanation, and what is considered background.
In his discussion of the discovery of the muon, he argues that the
calculation of Oppenheimer and Carlson, which showed that showers were
to be expected in the passage of electrons through matter, left the
penetrating particles, later shown to be muons, as the unexplained
phenomenon. Prior to their work, physicists thought the showering
particles were the problem, whereas the penetrating particles seemed
to be understood.



The role of theory as an "enabling theory," (i.e., one
that allows calculation or estimation of the size of the expected
effect and also the size of expected backgrounds) is also discussed by
Galison. (See also (Franklin 1995) and the discussion of the
Stern-Gerlach experiment below). Such a theory can help to determine
whether an experiment is feasible. Galison also emphasizes that
elimination of background that might simulate or mask an effect is
central to the experimental enterprise, and not a peripheral activity.
In the case of the weak neutral current experiments, the existence of
the currents depended crucially on showing that the event candidates
could not all be due to neutron
 background.[6]



There is also a danger that the design of an experiment may preclude
observation of a phenomenon. Galison points out that the original
design of one of the neutral current experiments, which included a
muon trigger, would not have allowed the observation of neutral
currents. In its original form the experiment was designed to observe
charged currents, which produce a high energy muon. Neutral currents
do not. Therefore, having a muon trigger precluded their observation.
Only after the theoretical importance of the search for neutral
currents was emphasized to the experimenters was the trigger changed.
Changing the design did not, of course, guarantee that neutral
currents would be observed.



Galison also shows that the theoretical presuppositions of the
experimenters may enter into the decision to end an experiment and
report the result. Einstein and de Haas ended their search for
systematic errors when their value for the gyromagnetic ratio of the
electron, \(g = 1\), agreed with their theoretical model of orbiting
electrons. This effect of presuppositions might cause one to be
skeptical of both experimental results and their role in theory
evaluation. Galison's history shows, however, that, in this
case, the importance of the measurement led to many repetitions of the
measurement. This resulted in an agreed-upon result that disagreed
with theoretical expectations.



Galison has eventually modified his views. In *Image and
Logic*, an extended study of instrumentation in 20th-century
high-energy physics, Galison (1997) has extended his argument that
there are two distinct experimental traditions within that
field--the visual (or image) tradition and the electronic (or
logic) tradition. The image tradition uses detectors such as cloud
chambers or bubble chambers, which provide detailed and extensive
information about each individual event. The electronic detectors used
by the logic tradition, such as geiger counters, scintillation
counters, and spark chambers, provide less detailed information about
individual events, but detect more events. Galison's view is
that experimenters working in these two traditions form distinct
epistemic and linguistic groups that rely on different forms of
argument. The visual tradition emphasizes the single
"golden" event. "On the image side resides a
deep-seated commitment to the 'golden event': the single
picture of such clarity and distinctness that it commands
acceptance." (Galison, 1997, p. 22) "The golden event was
the exemplar of the image tradition: an individual instance so
complete and well defined, so 'manifestly' free of
distortion and background that no further data had to be
involved" (p. 23). Because the individual events provided in the
logic detectors contained less detailed information than the pictures
of the visual tradition, statistical arguments based on large numbers
of events were required.



Kent Staley (1999) disagrees. He argues that the two traditions are
not as distinct as Galison believes:



> 
> I show that discoveries in both traditions have employed the same
> statistical [I would add "and/or probabilistic"] form of
> argument, even when basing discovery claims on single, golden events.
> Where Galison sees an epistemic divide between two communities that
> can only be bridged by creole- or pidgin-like
> 'interlanguage,' there is in fact a shared commitment to a
> statistical form of experimental argument. (p. 96).
> 



Staley believes that although there is certainly epistemic continuity
within a given tradition, there is also a continuity between the
traditions. This does not, I believe, mean that the shared commitment
comprises all of the arguments offered in any particular instance, but
rather that the same methods are often used by both communities.
Galison does not deny that statistical methods are used in the image
tradition, but he thinks that they are relatively unimportant.
"While statistics could certainly be used within the image
tradition, it was by no means necessary for most applications"
(Galison, 1997, p. 451). In contrast, Galison believes that arguments
in the logic tradition "were inherently and inalienably
statistical. Estimation of probable errors and the statistical excess
over background is not a side issue in these detectors--it is
central to the possibility of any demonstration at all" (p.
451).



Although a detailed discussion of the disagreement between Staley and
Galison would take us too far from the subject of this essay, they
both agree that arguments are offered for the correctness of
experimental results. Their disagreement concerns the nature of those
arguments. (For further discussion see Franklin, (2002), pp.
9-17).


### 2.2 The Case Against Learning From Experiment


#### 2.2.1 The Experimenters' Regress



H. Collins, A. Pickering, and others, have raised objections to the
view that experimental results are accepted on the basis of
epistemological arguments. They point out that "a sufficiently
determined critic can always find a reason to dispute any alleged
'result'" (MacKenzie 1989, p. 412). Harry Collins,
for example, is well known for his skepticism concerning both
experimental results and evidence. He develops an argument that he
calls the "experimenters' regress" (Collins 1985,
chapter 4, pp. 79-111): What scientists take to be a correct
result is one obtained with a good, that is, properly functioning,
experimental apparatus. But a good experimental apparatus is simply
one that gives correct results. Collins claims that there are no
formal criteria that one can apply to decide whether or not an
experimental apparatus is working properly. In particular, he argues
that calibrating an experimental apparatus by using a surrogate signal
cannot provide an independent reason for considering the apparatus to
be reliable.



In Collins' view the regress is eventually broken by negotiation
within the appropriate scientific community, a process driven by
factors such as the career, social, and cognitive interests of the
scientists, and the perceived utility for future work, but one that is
not decided by what we might call epistemological criteria, or
reasoned judgment. Thus, Collins concludes that his regress raises
serious questions concerning both experimental evidence and its use in
the evaluation of scientific hypotheses and theories. Indeed, if no
way out of the regress can be found, then he has a point.



Collins strongest candidate for an example of the experimenters'
regress is presented in his history of the early attempts to detect
gravitational radiation, or gravity waves. (For more detailed
discussion of this episode see (Collins 1985; 1994; Franklin 1994;
1997a) In this case, the physics community was forced to compare J.
Weber's claims that he had observed gravity waves with the
reports from six other experiments that failed to detect them. On the
one hand, Collins argues that the decision between these conflicting
experimental results could not be made on epistemological or
methodological grounds--he claims that the six negative
experiments could not legitimately be regarded as
 replications[7]
 and hence become less impressive. On the other hand, Weber's
apparatus, precisely because the experiments used a new type of
apparatus to try to detect a hitherto unobserved
 phenomenon,[8]
 could not be subjected to standard calibration techniques.



The results presented by Weber's critics were not only more
numerous, but they had also been carefully cross-checked. The groups
had exchanged both data and analysis programs and confirmed their
results. The critics had also investigated whether or not their
analysis procedure, the use of a linear algorithm, could account for
their failure to observe Weber's reported results. They had used
Weber's preferred procedure, a nonlinear algorithm, to analyze
their own data, and still found no sign of an effect. They had also
calibrated their experimental apparatuses by inserting acoustic pulses
of known energy and finding that they could detect a signal. Weber, on
the other hand, as well as his critics using his analysis procedure,
could not detect such calibration pulses.



There were, in addition, several other serious questions raised about
Weber's analysis procedures. These included an admitted
programming error that generated spurious coincidences between
Weber's two detectors, possible selection bias by Weber,
Weber's report of coincidences between two detectors when the
data had been taken four hours apart, and whether or not Weber's
experimental apparatus could produce the narrow coincidences
claimed.



It seems clear that the critics' results were far more credible
than Weber's. They had checked their results by independent
confirmation, which included the sharing of data and analysis
programs. They had also eliminated a plausible source of error, that
of the pulses being longer than expected, by analyzing their results
using the nonlinear algorithm and by explicitly searching for such
long
 pulses.[9]
 They had also calibrated their apparatuses by injecting pulses of
known energy and observing the output.



Contrary to Collins, I believe that the scientific community made a
reasoned judgment and rejected Weber's results and accepted
those of his critics. Although no formal rules were applied (e.g. if
you make four errors, rather than three, your results lack
credibility; or if there are five, but not six, conflicting results,
your work is still credible) the procedure was reasonable.



Pickering has argued that the reasons for accepting results are the
future utility of such results for both theoretical and experimental
practice and the agreement of such results with the existing community
commitments. In discussing the discovery of weak neutral currents,
Pickering states,



> 
> Quite simply, particle physicists accepted the existence of the
> neutral current because they could see how to ply their trade more
> profitably in a world in which the neutral current was real. (1984b,
> p. 87)
> 
> 
> Scientific communities tend to reject data that conflict with group
> commitments and, obversely, to adjust their experimental techniques to
> tune in on phenomena consistent with those commitments. (1981, p.
> 236)
> 
> 
> 



The emphasis on future utility and existing commitments is clear.
These two criteria do not necessarily agree. For example, there are
episodes in the history of science in which more opportunity for
future work is provided by the overthrow of existing theory. (See, for
example, the history of the overthrow of parity conservation and of CP
symmetry discussed below and in Franklin 1986, Ch. 1, 3.)


#### 2.2.2 Communal Opportunism and Plastic Resources



Pickering offered a different view of experimental results in late
1980s. In his view the material procedure (including the experimental
apparatus itself along with setting it up, running it, and monitoring
its operation), the theoretical model of that apparatus, and the
theoretical model of the phenomena under investigation are all plastic
resources that the investigator brings into relations of mutual
support. (Pickering 1987; Pickering 1989). He says:



> 
> Achieving such relations of mutual support is, I suggest, the defining
> characteristic of the successful experiment. (1987, p. 199)
> 



He uses Morpurgo's search for free quarks, or fractional charges
of \(\tfrac{1}{3} e\) or \(\tfrac{2}{3} e\), where \(e\) is the charge
of the electron. (See also Gooding 1992.) Morpurgo used a modern
Millikan-type apparatus and initially found a continuous distribution
of charge values. Following some tinkering with the apparatus,
Morpurgo found that if he separated the capacitor plates he obtained
only integral values of charge. "After some theoretical
analysis, Morpurgo concluded that he now had his apparatus working
properly, and reported his failure to find any evidence for fractional
charges" (Pickering 1987, p. 197).



Pickering goes on to note that Morpurgo did not tinker with the two
competing theories of the phenomena then on offer, those of integral
and fractional charge:



> 
> The initial source of doubt about the adequacy of the early stages of
> the experiment was precisely the fact that their
> findings--continuously distributed charges--were consonant
> with neither of the phenomenal models which Morpurgo was prepared to
> countenance. And what motivated the search for a new instrumental
> model was Morpurgo's eventual success in producing findings in
> accordance with one of the phenomenal models he was willing to accept
> 
> 
> The conclusion of Morpurgo's first series of experiments, then,
> and the production of the observation report which they sustained, was
> marked by bringing into relations of mutual support of the three
> elements I have discussed: the material form of the apparatus and the
> two conceptual models, one instrumental and the other phenomenal.
> Achieving such relations of mutual support is, I suggest, the defining
> characteristic of the successful experiment. (p. 199)
> 
> 
> 



Pickering has made several important and valid points concerning
experiment. Most importantly, he has emphasized that an experimental
apparatus is initially rarely capable of producing a valid
experimental results and that some adjustment, or tinkering, is
required before it does. He has also recognized that both the theory
of the apparatus and the theory of the phenomena can enter into the
production of a valid experimental result. What one may question,
however, is the emphasis he places on these theoretical components.
From Millikan onwards, experiments had strongly supported the
existence of a fundamental unit of charge and charge quantization. The
failure of Morpurgo's apparatus to produce measurements of
integral charge indicated that it was not operating properly and that
his theoretical understanding of it was faulty. It was the failure to
produce measurements in agreement with what was already known (i.e.,
the failure of an important experimental check) that caused doubts
about Morpurgo's measurements. This was true regardless of the
theoretical models available, or those that Morpurgo was willing to
accept. It was only when Morpurgo's apparatus could reproduce
known measurements that it could be trusted and used to search for
fractional charge. To be sure, Pickering has allowed a role for the
natural world in the production of the experimental result, but it
does not seem to be decisive.


#### 2.2.3 Critical Responses



Ackermann has offered a modification of Pickering's view. He
suggests that the experimental apparatus itself is a less plastic
resource then either the theoretical model of the apparatus or that of
the phenomenon.



> 
> To repeat, changes in \(A\) [the apparatus] can often be seen (in real
> time, without waiting for accommodation by \(B\) [the theoretical
> model of the apparatus]) as improvements, whereas
> 'improvements' in \(B\) don't begin to count unless
> \(A\) is actually altered and realizes the improvements conjectured.
> It's conceivable that this small asymmetry can account,
> ultimately, for large scale directions of scientific progress and for
> the objectivity and rationality of those directions. (Ackermann 1991,
> p. 456)
> 



Hacking (1992) has also offered a more complex version of
Pickering's later view. He suggests that the results of mature
laboratory science achieve stability and are self-vindicating when the
elements of laboratory science are brought into mutual consistency and
support. These are (1) ideas: questions, background knowledge,
systematic theory, topical hypotheses, and modeling of the apparatus;
(2) things: target, source of modification, detectors, tools, and data
generators; and (3) marks and the manipulation of marks: data, data
assessment, data reduction, data analysis, and interpretation.



> 
> Stable laboratory science arises when theories and laboratory
> equipment evolve in such a way that they match each other and are
> mutually self-vindicating. (1992, p. 56)
> 
> 
> We invent devices that produce data and isolate or create phenomena,
> and a network of different levels of theory is true to these
> phenomena. Conversely we may in the end count them only as phenomena
> only when the data can be interpreted by theory. (pp. 57-8)
> 
> 
> 



One might ask whether such mutual adjustment between theory and
experimental results can always be achieved? What happens when an
experimental result is produced by an apparatus on which several of
the epistemological strategies, discussed earlier, have been
successfully applied, and the result is in disagreement with our
theory of the phenomenon? Accepted theories can be refuted. Several
examples will be presented below.



Hacking himself worries about what happens when a laboratory science
that is true to the phenomena generated in the laboratory, thanks to
mutual adjustment and self-vindication, is successfully applied to the
world outside the laboratory. Does this argue for the truth of the
science. In Hacking's view it does not. If laboratory science
does produce happy effects in the "untamed world,... it is
not the truth of anything that causes or explains the happy
effects" (1992, p. 60).


#### 2.2.4 The Dance of Agency



Pickering offered yet another, a somewhat revised account of science.
"My basic image of science is a performative one, in which the
performances the doings of human and material agency come to the fore.
Scientists are human agents in a field of material agency which they
struggle to capture in machines (Pickering, 1995, p. 21)." He
then discusses the complex interaction between human and material
agency, which I interpret as the interaction between experimenters,
their apparatus, and the natural world.



> 
> The dance of agency, seen asymmetrically from the human end, thus
> takes the form of a *dialectic of resistance and
> accommodations,* where resistance denotes the failure to achieve
> an intended capture of agency in practice, and accommodation an active
> human strategy of response to resistance, which can include revisions
> to goals and intentions as well as to the material form of the machine
> in question and to the human frame of gestures and social relations
> that surround it (p. 22)."
> 



Pickering's idea of resistance is illustrated by
Morpurgo's observation of continuous, rather than integral or
fractional, electrical charge, which did not agree with his
expectations. Morpurgo's accommodation consisted of changing his
experimental apparatus by using a larger separation between his
plates, and also by modifying his theoretical account of the
apparatus. That being done, integral charges were observed and the
result stabilized by the mutual agreement of the apparatus, the theory
of the apparatus, and the theory of the phenomenon. Pickering notes
that "the outcomes depend on how the world is (p. 182)."
"In this way, then, *how the material world is* leaks
into and infects our representations of it in a nontrivial and
consequential fashion. My analysis thus displays an intimate and
responsive engagement between scientific knowledge and the material
world that is integral to scientific practice (p. 183)."



Nevertheless there is something confusing about Pickering's
invocation of the natural world. Although Pickering acknowledges the
importance of the natural world, his use of the term
"infects" seems to indicate that he isn't entirely
happy with this. Nor does the natural world seem to have much
efficacy. It never seems to be decisive in any of Pickering's
case studies. Recall that he argued that physicists accepted the
existence of weak neutral currents because "they could ply their
trade more profitably in a world in which the neutral current was
real." In his account, Morpurgo's observation of
continuous charge is important only because it disagrees with his
theoretical models of the phenomenon. The fact that it disagreed with
numerous previous observations of integral charge doesn't seem
to matter. This is further illustrated by Pickering's discussion
of the conflict between Morpurgo and Fairbank. As we have seen,
Morpurgo reported that he did not observe fractional electrical
charges. On the other hand, in the late 1970s and early 1980s,
Fairbank and his collaborators published a series of papers in which
they claimed to have observed fractional charges (See, for example,
LaRue, Phillips et al. 1981 ). Faced with this discord Pickering
concludes,



> 
> In Chapter 3, I traced out Morpurgo's route to his findings in
> terms of the particular vectors of cultural extension that he pursued,
> the particular resistances and accommodations thus precipitated, and
> the particular interactive stabilizations he achieved. The same could
> be done, I am sure, in respect of Fairbank. And these tracings are all
> that needs to said about their divergence. It just happened that the
> contingencies of resistance and accommodation worked out differently
> in the two instances. Differences like these are, I think, continually
> bubbling up in practice, without any special causes behind them (pp.
> 211-212).
> 



The natural world seems to have disappeared from Pickering's
account. There is a real question here as to whether or not fractional
charges exist in nature. The conclusions reached by Fairbank and by
Morpurgo about their existence cannot both be correct. It seems
insufficient to merely state, as Pickering does, that Fairbank and
Morpurgo achieved their individual stabilizations and to leave the
conflict unresolved. (Pickering does comment that one could follow the
subsequent history and see how the conflict was resolved, and he does
give some brief statements about it, but its resolution is not
important for him). At the very least one should consider the actions
of the scientific community. Scientific knowledge is not determined
individually, but communally. Pickering seems to acknowledge this.
"One might, therefore, want to set up a metric and say that
items of scientific knowledge are more or less objective depending on
the extent to which they are threaded into the rest of scientific
culture, socially stabilized over time, and so on. I can see nothing
wrong with thinking this way.... (p. 196)." The fact that
Fairbank believed in the existence of fractional electrical charges,
or that Weber strongly believed that he had observed gravity waves,
does not make them right. These are questions about the natural world
that can be resolved. Either fractional charges and gravity waves
exist or they don't, or to be more cautious we might say that we
have good reasons to support our claims about their existence, or we
do not.



Another issue neglected by Pickering is the question of whether a
particular mutual adjustment of theory, of the apparatus or the
phenomenon, and the experimental apparatus and evidence is justified.
Pickering seems to believe that any such adjustment that provides
stabilization, either for an individual or for the community, is
acceptable. Others disagree. They note that experimenters sometimes
exclude data and engage in selective analysis procedures in producing
experimental results. These practices are, at the very least,
questionable as is the use of the results produced by such practices
in science. There are, in fact, procedures in the normal practice of
science that provide safeguards against them. (For details see
Franklin, 2002, Section 1).



The difference in attitudes toward the resolution of discord is one of
the important distinctions between Pickering's and
Franklin's view of science. Franklin remarks that it is
insufficient simply to say that the resolution is socially stabilized.
The important question is how that resolution was achieved and what
were the reasons offered for that resolution. If we are faced with
discordant experimental results and both experimenters have offered
reasonable arguments for their correctness, then clearly more work is
needed. It seems reasonable, in such cases, for the physics community
to search for an error in one, or both, of the experiments.



Pickering discusses yet another difference between his view and that
of Franklin. Pickering sees traditional philosophy of science as
regarding objectivity "as stemming from a peculiar kind of
mental hygiene or policing of thought. This police function relates
specifically to theory choice in science, which,... is usually
discussed in terms of the rational rules or methods responsible for
closure in theoretical debate (p. 197)." He goes on to remark
that,



> 
> The most action in recent methodological thought has centered on
> attempts like Allan Franklin's to extend the methodological
> approach to experiments by setting up a set of rules for their proper
> performance. Franklin thus seeks to extend classical discussions of
> objectivity to the empirical base of science (a topic hitherto
> neglected in the philosophical tradition but one that, of course the
> mangle [Pickering's view] also addresses). For an argument
> between myself and Franklin on the same lines as that laid out below,
> see (Franklin 1990, Chapter 8; Franklin 1991); and (Pickering 1991);
> and for commentaries related to that debate, (Ackermann 1991) and
> (Lynch 1991) (p. 197)."
> 



For further discussion see Franklin 1993b. Although
Franklin's epistemology of experiment is designed to offer good
reasons for belief in experimental results, they are not a set of
rules. Franklin regards them as a set of strategies, from which
physicists choose, in order to argue for the correctness of their
results. As noted above, the strategies offered are neither exclusive
or exhaustive.



There is another point of disagreement between Pickering and Franklin.
Pickering claims to be dealing with the practice of science, and yet
he excludes certain practices from his discussions. One scientific
practice is the application of the epistemological strategies outlined
above to argue for the correctness of an experimental results. In
fact, one of the essential features of an experimental paper is the
presentation of such arguments. Writing such papers, a performative
act, is also a scientific practice and it would seem reasonable to
examine both the structure and content of those papers.


#### 2.2.5 Hacking's 'The Social Construction of What'?



Ian Hacking (1999, chapter 3) provided an incisive and interesting
discussion of the issues that divide the constructivists (Collins,
Pickering, etc.) from the rationalists (Stuewer, Franklin, Buchwald,
etc.). He sets out three sticking points between the two views: 1)
contingency, 2) nominalism, and 3) external explanations of
stability.



Contingency is the idea that science is not predetermined, that it
could have developed in any one of several successful ways. This is
the view adopted by constructivists. Hacking illustrates this with
Pickering's account of high-energy physics during the 1970s
during which the quark model came to dominate. (See Pickering
1984a).



> 
> The constructionist maintains a contingency thesis. In the case of
> physics, (a) physics theoretical, experimental, material) could have
> developed in, for example, a nonquarky way, and, by the detailed
> standards that would have evolved with this alternative physics, could
> have been as successful as recent physics has been by its detailed
> standards. Moreover, (b) there is no sense in which this imagined
> physics would be equivalent to present physics. The physicist denies
> that. (Hacking 1999, pp. 78-79).
> 
> 
> To sum up Pickering's doctrine: there could have been a research
> program as successful ("progressive") as that of
> high-energy physics in the 1970s, but with different theories,
> phenomenology, schematic descriptions of apparatus, and apparatus, and
> with a different, and progressive, series of robust fits between these
> ingredients. Moreover and this is something badly in need of
> clarification the "different" physics would not have been
> equivalent to present physics. Not logically incompatible with, just
> different.
> 
> 
> 
> The constructionist about (the idea) of quarks thus claims that the
> upshot of this process of accommodation and resistance is not fully
> predetermined. Laboratory work requires that we get a robust fit
> between apparatus, beliefs about the apparatus, interpretations and
> analyses of data, and theories. *Before a robust fit has been
> achieved, it is not determined what that fit will be. Not determined
> by how the world is, not determined by technology now in existence,
> not determined by the social practices of scientists, not determined
> by interests or networks, not determined by genius, not determined by
> anything* (pp. 72-73, emphasis added).
> 
> 
> 



Much depends here on what Hacking means by "determined."
If he means entailed then one must agree with him. It is doubtful that
the world, or more properly, what we can learn about it, entails a
unique theory. If not, as seems more plausible, he means that the way
the world is places no restrictions on that successful science, then
the rationalists disagree strongly. They want to argue that the way
the world is restricts the kinds of theories that will fit the
phenomena, the kinds of apparatus we can build, and the results we can
obtain with such apparatuses. To think otherwise seems silly. Consider
a homey example. It seems highly unlikely that someone can come up
with a successful theory in which objects whose density is greater
than that of air fall upwards. This is not a caricature of the view
Hacking describes. Describing Pickering's view, he states,
"Physics did not need to take a route that involved
Maxwell's Equations, the Second Law of Thermodynamics, or the
present values of the velocity of light (p. 70)." Although one
may have some sympathy for this view as regards Maxwell's
Equations or the Second Law of Thermodynamics, one may not agree about
the value of the speed of light. That is determined by the way the
world is. Any successful theory of light must give that value for its
speed.



At the other extreme are the "inevitablists," among whom
Hacking classifies most scientists. He cites Sheldon Glashow, a Nobel
Prize winner, "Any intelligent alien anywhere would have come
upon the same logical system as we have to explain the structure of
protons and the nature of supernovae (Glashow 1992, p. 28)."



Another difference between Pickering and Franklin on contingency
concerns the question of not whether an alternative is possible, but
rather whether there are reasons why that alternative should be
pursued. Pickering seems to identify *can* with
*ought*.



In the late 1970s there was a disagreement between the results of
low-energy experiments on atomic parity violation (the violation of
left-right symmetry) performed at the University of Washington and at
Oxford University and the result of a high-energy experiment on the
scattering of polarized electrons from deuterium (the SLAC E122
experiment). The atomic-parity violation experiments failed to observe
the parity-violating effects predicted by the Weinberg- Salam (W-S)
unified theory of electroweak interactions, whereas the SLAC
experiment observed the predicted effect. These early atomic physics
results were quite uncertain in themselves and that uncertainty was
increased by positive results obtained in similar experiments at
Berkeley and Novosibirsk. At the time the theory had other evidential
support, but was not universally accepted. Pickering and Franklin are
in agreement that the W-S theory was accepted on the basis of the SLAC
E122 result. They differ dramatically in their discussions of the
experiments. Their difference on contingency concerns a particular
theoretical alternative that was proposed at the time to explain the
discrepancy between the experimental results.



Pickering asked why a theorist might not have attempted to find a
variant of electroweak gauge theory that might have reconciled the
Washington-Oxford atomic parity results with the positive E122 result.
(What such a theorist was supposed to do with the supportive atomic
parity results later provided by experiments at Berkeley and at
Novosibirsk is never mentioned). "But though it is true that
E122 analysed their data in a way that displayed the improbability
[the probability of the fit to the hybrid model was 6 x
10[?]4] of a particular class of variant gauge
theories, the so-called 'hybrid models,' I do not believe
that it would have been impossible to devise yet more variants"
(Pickering 1991, p. 462). Pickering notes that open-ended recipes for
constructing such variants had been written down as early as 1972 (p.
467). It would have been possible to do so, but one may ask whether or
not a scientist might have wished to do so. If the scientist agreed
with Franklin's view that the SLAC E122 experiment provided
considerable evidential weight in support of the W-S theory and that a
set of conflicting and uncertain results from atomic parity-violation
experiments gave an equivocal answer on that support, what reason
would they have had to invent an alternative?



This is not to suggest that scientists do not, or should not, engage
in speculation, but rather that there was no necessity to do so in
this case. Theorists often do propose alternatives to existing,
well-confirmed theories.



Constructivist case studies always seem to result in the support of
existing, accepted theory (Pickering 1984a; 1984b; 1991; Collins 1985;
Collins and Pinch 1993). One criticism implied in such cases is that
alternatives are not considered, that the hypothesis space of
acceptable alternatives is either very small or empty. One may
seriously question this. Thus, when the experiment of Christenson
*et al*. (1964) detected \(\ce{K2^0}\) decay into two pions,
which seemed to show that CP symmetry (combined particle-antiparticle
and space inversion symmetry) was violated, no fewer than 10
alternatives were offered. These included (1) the cosmological model
resulting from the local dysymmetry of matter and antimatter, (2)
external fields, (3) the decay of the \(\ce{K2^0}\) into a
\(\ce{K1^0}\) with the subsequent decay of the \(\ce{K1^0}\)into two
pions, which was allowed by the symmetry, (4) the emission of another
neutral particle, "the paritino," in the \(\ce{K2^0}\)
decay, similar to the emission of the neutrino in beta decay, (5) that
one of the pions emitted in the decay was in fact a
"spion," a pion with spin one rather than zero, (6) that
the decay was due to another neutral particle, the L, produced
coherently with the \(\ce{K^0}\), (7) the existence of a
"shadow" universe, which interacted with out universe only
through the weak interactions, and that the decay seen was the decay
of the "shadow \(\ce{K2^0}\)," (8) the failure of the
exponential decay law, 9) the failure of the principle of
superposition in quantum mechanics, and 10) that the decay pions were
not bosons.



As one can see, the limits placed on alternatives were not very
stringent. By the end of 1967, all of the alternatives had been tested
and found wanting, leaving CP symmetry unprotected. Here the differing
judgments of the scientific community about what was worth proposing
and pursuing led to a wide variety of alternatives being tested.



Hacking's second sticking point is nominalism, or name-ism. He
notes that in its most extreme form nominalism denies that there is
anything in common or peculiar to objects selected by a name, such as
"Douglas fir" other than that they are called Douglas fir.
Opponents contend that good names, or good accounts of nature, tell us
something correct about the world. This is related to the
realism-antirealism debate concerning the status of unobservable
entities that has plagued philosophers for millennia. For example Bas
van Fraassen (1980), an antirealist, holds that we have no grounds for
belief in unobservable entities such as the electron and that
accepting theories about the electron means only that we believe that
the things the theory says about observables is true. A realist claims
that electrons really exist and that as, for example, Wilfred Sellars
remarked, "to have good reason for holding a theory is *ipso
facto* to have good reason for holding that the entities
postulated by the theory exist (Sellars 1962, p. 97)." In
Hacking's view a scientific nominalist is more radical than an
antirealist and is just as skeptical about fir trees as they are about
electrons. A nominalist further believes that the structures we
conceive of are properties of our representations of the world and not
of the world itself. Hacking refers to opponents of that view as
inherent structuralists.



Hacking also remarks that this point is related to the question of
"scientific facts." Thus, constructivists Latour and
Woolgar originally entitled their book *Laboratory Life: The Social
Construction of Scientific Facts* (1979). Andrew Pickering
entitled his history of the quark model *Constructing Quarks*
(Pickering 1984a). Physicists argue that this demeans their work.
Steven Weinberg, a realist and a physicist, criticized
Pickering's title by noting that no mountaineer would ever name
a book *Constructing Everest*. For Weinberg, quarks and Mount
Everest have the same ontological status. They are both facts about
the world. Hacking argues that constructivists do not, despite
appearances, believe that facts do not exist, or that there is no such
thing as reality. He cites Latour and Woolgar "that
'out-there-ness' is a *consequence* of scientific
work rather than its cause (Latour and Woolgar 1986, p. 180)."
Hacking reasonably concludes that,



> 
> Latour and Woolgar were surely right. We should not *explain*
> why some people believe that \(p\) by saying that \(p\) is true, or
> corresponds to a fact, or the facts. For example: someone believes
> that the universe began with what for brevity we call a big bang. A
> host of reasons now supports this belief. But after you have listed
> all the reasons, you should not add, as if it were an additional
> reason for believing in the big bang, 'and it is true that the
> universe began with a big bang.' Or 'and it is a
> fact.'This observation has nothing peculiarly to do with social
> construction. It could equally have been advanced by an old-fashioned
> philosopher of language. It is a remark about the grammar of the verb
> 'to explain' (Hacking 1999, pp. 80-81).
> 



One might add, however, that the reasons Hacking cites as supporting
that belief are given to us by valid experimental evidence and not by
the social and personal interests of scientists. Latour and Woolgar
might not agree. Franklin argues that we have good reasons to believe
in facts, and in the entities involved in our theories, always
remembering, of course, that science is fallible.



Hacking's third sticking point is the external explanations of
stability.



> 
> The constructionist holds that explanations for the stability of
> scientific belief involve, at least in part, elements that are
> external to the content of science. These elements typically include
> social factors, interests, networks, or however they be described.
> Opponents hold that whatever be the context of discovery, the
> explanation of stability is internal to the science itself (Hacking
> 1999, p. 92).
> 
> 
> Rationalists think that most science proceeds as it does in the light
> of good reasons produced by research. Some bodies of knowledge become
> stable because of the wealth of good theoretical and experimental
> reasons that can be adduced for them. Constructivists think that the
> reasons are not decisive for the course of science. Nelson (1994)
> concludes that this issue will never be decided. Rationalists, at
> least retrospectively, can always adduce reasons that satisfy them.
> Constructivists, with equal ingenuity, can always find to their own
> satisfaction an openness where the upshot of research is settled by
> something other than reason. Something external. That is one way of
> saying we have found an irresoluble "sticking point" (pp.
> 91-92)
> 
> 
> 



Thus, there is a rather severe disagreement on the reasons for the
acceptance of experimental results. For some, like Staley, Galison and
Franklin, it is because of epistemological arguments. For others, like
Pickering, the reasons are utility for future practice and agreement
with existing theoretical commitments. Although the history of science
shows that the overthrow of a well-accepted theory leads to an
enormous amount of theoretical and experimental work, proponents of
this view seem to accept it as unproblematical that it is always
agreement with existing theory that has more future utility. Hacking
and Pickering also suggest that experimental results are accepted on
the basis of the mutual adjustment of elements which includes the
theory of the phenomenon.



Nevertheless, everyone seems to agree that a consensus does arise on
experimental results.


### 2.3 Measuring, Calibrating, Predicting



We have encountered (Section 2.2.1) Franklin's definition of
calibration as the use of a surrogate signal that has been established
independently of the apparatus being calibrated, or as the
reproduction of independently (on an independent apparatus) well
established phenomena. He used this account in order to argue against
Collins's view of the viciousness of the experimenter's
regress. Yet other accounts of calibration explaining the process of
measurement evoke similar worries.



E. Tal defines calibration as "the activity of establishing a
correlation between indications of a measuring instrument and quantity
values associated with a measurement standard" (Tal 2017a, 243).
Mere "instrument indications" (Tal 2017a) become
"measurement outcomes" when interpreted in a larger
context of theoretical background and calibration of the measuring
instrument. Yet Boyd (2021, 43) worries that this leaves the
measurement open to the vicious regress akin to the
experimenter's regress H. Collins has argued for (see Section
2.2.1), since the experimenters do not "have access to
true values of the measurand [i.e., whatever is measured] to use as
standards of calibration".



The regress may be blocked by comparisons across measuring outcomes
performed in differently modeled measurements, i.e. across different
measurement contexts (the context being constituted by intricacies of
the operational and theoretical background of apparata). (Tal 2017a,
239) These different contexts are idealized and then compared in order
to establish whether they cohere to the predictions concerning the
measurand. Thus, calibration is "the activity of modeling
different processes and testing the consequences of such models for
mutual compatibility" (Tal 2017a, 246). An act of calibration is
effectively the comparison of idealized models across measuring
processes, where an act of measurement becomes justified by the
models' mutual coherence.



Boyd (2021, 46) states that idealizations of measurement processes
cannot provide the foundation for objective measurement since
idealizations strip the context of its key details. In fact, the
measurement has an epistemic utility by virtue of the
context-sensitive details. The measurement outcomes gain epistemic
value only as "enriched evidence", i.e., in the wider
empirical and theoretical context.



Moreover, Tal's view conflates prediction and calibration (Boyd
2021, 48) taking us back to the viciousness of the
experimenter's regress. Thus, "Calibration was supposed to
disrupt the regress because an instrument could be judged to be
working correctly in virtue of something other than success at its
principal aim" (Boyd 2021, 48). Calibration has to provide a
point outside the web of cohering predictions if it is to break the
regress, e.g. by the subtle processing of instrument indications.



Progressive coherentism's attempted way out of the vicious
regress, as proposed by Hasok Chang (2004, 2007), points to a
historical trajectory of the development of measuring procedures and
calibration. The web of cohering measuring process is dynamic: it
unfolds in time as a spiral. And the measurement process that
initially aims at prediction eventually becomes a result used for
calibrating processes. Yet, such spiraling progress may be just an
elaborate dynamic coherence web of Collins' type where
inter-subjective agreement is the foundation, if other non-empirical
virtues such as "creative achievement" play as important
role as the empirical ones as claimed by Chang (2007). If so,
calibration does not offer an independent leverage to the measurement
outcomes after all.



Perovic (2017) analyzes in-situ calibration procedures in the
Large Hadron Collider pointing out that calibration serves as an
epistemic leverage of Franklin's type during the commissioning
phase of the experimental apparatus. But various calibration
procedures continue all along and gradually feed into the measurement
itself during the entire measurement process. Boyd (2021) further
explores commissioning procedures and the gradual transition from
"engineering data" to "science data", where
criteria of prediction significantly change. The apparatus initially
relies on the existing well-known data but then coherence with other
apparata that Tal insists on becomes increasingly less significant in
justifying the measurement outcomes.


### 2.4 Big Science Physics: Theory-ladenness in High Energy Physics



Authors like Thomas Kuhn and Paul Feyerabend put forward the view that
evidence does not confirm or refute a scientific theory since it is
laden by it. Evidence is not a set of observational sentences
autonomous from theoretical ones, as logical positivists believed.
Each new theory or a theoretical paradigm, as Kuhn labeled larger
theoretical frameworks, produces, as it were, evidence anew.



Thus, theoretical concepts infect the entire experimental process from
the stage of design and preparation to the production and analysis of
data. A simple example that is supposed to convincingly illustrate
this view are measurements of temperature with a mercury thermometer
one uses in order to test whether objects expand when their
temperature increases. Note that in such a case one tests the
hypothesis by relying on the very assumption that the expansion of
mercury indicates increase in temperature.



There may be a fairly simple way out of the vicious circle in which
theory and experiment are caught in this particular case of
theory-ladenness. It may suffice to calibrate the mercury thermometer
with a constant volume gas thermometer, for example, where its use
does not rely on the tested hypothesis but on the proportionality of
the pressure of the gas and its absolute temperature (Franklin et al.
1989).



Although most experiments are far more complex than this toy example,
one could certainly approach the view that experimental results are
theory-laden on a case-by-case basis. Yet there may be a more general
problem with the view.



Bogen and Woodward (1988) argued that debate on the relationship
between theory and observation overlooks a key ingredient in the
production of experimental evidence, namely the experimental
phenomena. The experimentalists distill experimental phenomena from
raw experimental data (e.g. electronic or digital tracks in particle
colliders) using various tools of statistical analysis. Thus,
identification of an experimental phenomenon as significant (e.g. a
peak at a particular energy of colliding beams) is free of the theory
that the experiment may be designed to test (e.g. the prediction of a
particular particle). Only when significant phenomenon has been
identified can a stage of data analysis begin in which the phenomenon
is deemed to either support or refute a theory. Thus, the
theory-ladenness of evidence thesis fails at least in some experiments
in physics.



The authors substantiate their argument in part through an analysis of
experiments that led to a breakthrough discovery of weak neutral
currents. It is a type of force produced by so-called bosons --
short-lived particles responsible for energy transfer between other
particles such as hadrons and leptons. The relevant peaks were
recognized as significant via statistical analysis of data, and later
on interpreted as evidence for the existence of the bosons.



This view and the case study have been challenged by Schindler (2011).
He argues that the tested theory was critical in the assessment of the
reliability of data in the experiments with weak neutral currents. He
also points out that, on occasion, experimental data can even be
ignored if they are deemed irrelevant from a theoretical perspective
that physicists find particularly compelling. This was the case in
experiments with so-called zebra pattern magnetic anomalies on the
ocean floor. The readings of new apparatuses used to scan the ocean
floor produced intriguing signals. Yet the researchers could not
interpret these signals meaningfully or satisfyingly distinguish them
from noise unless they relied on some theoretical account of both the
structure of the ocean floor and the earth's magnetic field.



Karaca (2013) points out that a crude theory-observation distinction
is particularly unhelpful in understanding high-energy physics
experiments. It fails to capture the complexity of relevant
theoretical structures and their relation to experimental data.
Theoretical structures can be composed of background, model, and
phenomenological theories. Background theories are very general
theories (e.g. quantum field theory or quantum electrodynamics) that
define the general properties of physical particles and their
interactions. Models are specific instances of background theories
that define particular particles and their properties. While
phenomenological theories develop testable predictions based on these
models.



Now, each of these theoretical segments stands in a different
relationship to experimental data--the experiments can be laden
by a different segment to a different extent. This requires a nuanced
categorization of theory-ladeness, from weak to strong.



Thus, an experimental apparatus can be designed to test a very
specific theoretical model. UA1 and UA2 detectors at CERN's
Super Proton Synchrotron were designed to detect particles only in a
very specific energy regime in which W and Z bosons of the Standard
Model were expected to exist.



In contrast, exploratory experiments approach phenomena without
relying on a particular theoretical model. Thus, sometimes a
theoretical framework for an experiment consists of phenomenological
theory alone. Karaca argues that experiments with deep-inelastic
electron-proton scattering in the late 1960s and early 1970s are
example of such weakly theory-laden experiments. The application of
merely phenomenological parameters in the experiment resulted in the
very important discovery of the composite rather than point-like
structure of hadrons (protons and neutrons), or the so-called scaling
law. And this eventually led to a successful theoretical model of the
composition of hadrons, namely quantum chromodynamics, or the
quark-model of strong interactions.


## 3. The Roles of Experiment


### 3.1 A Life of Its Own



Although experiment often takes its importance from its relation to
theory, Hacking pointed out that it often has a life of its own,
independent of theory. He notes the pristine observations of Carolyn
Herschel's discovery of comets, William Herschel's work on
"radiant heat," and Davy's observation of the gas
emitted by algae and the flaring of a taper in that gas. In none of
these cases did the experimenter have any theory of the phenomenon
under investigation. One may also note the nineteenth century
measurements of atomic spectra and the work on the masses and
properties on elementary particles during the 1960s. Both of these
sequences were conducted without any guidance from theory.



In deciding what experimental investigation to pursue, scientists may
very well be influenced by the equipment available and their own
ability to use that equipment (McKinney 1992). Thus, when the
Mann-O'Neill collaboration was doing high energy physics
experiments at the Princeton-Pennsylvania Accelerator during the late
1960s, the sequence of experiments was (1) measurement of the
\(\ce{K+}\) decay rates, (2) measurement of the \(\ce{K+\_{e 3}}\)
branching ratio and decay spectrum, (3) measurement of the \(\ce{K+\_{e
2}}\) branching ratio, and (4) measurement of the form factor in
\(\ce{K+\_{e 3}}\) decay. These experiments were performed with
basically the same experimental apparatus, but with relatively minor
modifications for each particular experiment. By the end of the
sequence the experimenters had become quite expert in the use of the
apparatus and knowledgeable about the backgrounds and experimental
problems. This allowed the group to successfully perform the
technically more difficult experiments later in the sequence. We might
refer to this as "instrumental loyalty" and the
"recycling of expertise" (Franklin 1997b). This meshes
nicely with Galison's view of experimental traditions.
Scientists, both theorists and experimentalists, tend to pursue
experiments and problems in which their training and expertise can be
used.



Hacking also remarks on the "noteworthy observations" on
Iceland Spar by Bartholin, on diffraction by Hooke and Grimaldi, and
on the dispersion of light by Newton. "Now of course Bartholin,
Grimaldi, Hooke, and Newton were not mindless empiricists without an
'idea' in their heads. They saw what they saw because they
were curious, inquisitive, reflective people. They were attempting to
form theories. But in all these cases it is clear that the
observations preceded any formulation of theory" (Hacking 1983,
p. 156). In all of these cases we may say that these were observations
waiting for, or perhaps even calling for, a theory. The discovery of
any unexpected phenomenon calls for a theoretical explanation.


### 3.2 Confirmation and Refutation



Nevertheless several of the important roles of experiment involve its
relation to theory. Experiment may confirm a theory, refute a theory,
or give hints to the mathematical structure of a theory.


#### 3.2.1 A Crucial Experiment: The Discovery of Parity Nonconservation



Let us consider first an episode in which the relation between theory
and experiment was clear and straightforward. This was a
"crucial" experiment, one that decided unequivocally
between two competing theories, or classes of theory. The episode was
that of the discovery that parity, mirror-reflection symmetry or
left-right symmetry, is not conserved in the weak interactions. (For
details of this episode see Franklin (1986, Ch. 1) and
 Appendix 1).
 Experiments showed that in the beta decay of nuclei the number of
electrons emitted in the same direction as the nuclear spin was
different from the number emitted opposite to the spin direction. This
was a clear demonstration of parity violation in the weak
interactions.


#### 3.2.2 A Persuasive Experiment: The Discovery of CP Violation



After the discovery of parity and charge conjugation nonconservation,
and following a suggestion by Landau, physicists considered CP
(combined parity and particle-antiparticle symmetry), which was still
conserved in the experiments, as the appropriate symmetry. One
consequence of this scheme, if CP were conserved, was that the
\(\ce{K1^0}\) meson could decay into two pions, whereas the
\(\ce{K2^0}\) meson could
 not.[10]
 Thus, observation of the decay of \(\ce{K2^0}\) into two pions would
indicate CP violation. The decay was observed by a group at Princeton
University. Although several alternative explanations were offered,
experiments eliminated each of the alternatives leaving only CP
violation as an explanation of the experimental result. (For details
of this episode see Franklin (1986, Ch. 3) and
 Appendix 2.)


#### 3.2.3 Confirmation After 70 Years: The Discovery of Bose-Einstein Condensation



In both of the episodes discussed previously, those of parity
nonconservation and of CP violation, we saw a decision between two
competing classes of theories. This episode, the discovery of
Bose-Einstein condensation (BEC), illustrates the confirmation of a
specific theoretical prediction 70 years after the theoretical
prediction was first made. Bose (1924) and Einstein (1924; 1925)
predicted that a gas of noninteracting bosonic atoms will, below a
certain temperature, suddenly develop a macroscopic population in the
lowest energy quantum
 state.[11]
 (For details of this episode see
 Appendix 3.)


### 3.3 Complications



In the three episodes discussed in the previous section, the relation
between experiment and theory was clear. The experiments gave
unequivocal results and there was no ambiguity about what theory was
predicting. None of the conclusions reached has since been questioned.
Parity and CP symmetry are violated in the weak interactions and
Bose-Einstein condensation is an accepted phenomenon. In the practice
of science things are often more complex. Experimental results may be
in conflict, or may even be incorrect. Theoretical calculations may
also be in error or a correct theory may be incorrectly applied. There
are even cases in which both experiment and theory are wrong. As noted
earlier, science is fallible. In this section I will discuss several
episodes which illustrate these complexities.


#### 3.3.1 The Fall of the Fifth Force



The episode of the fifth force is the case of a refutation of an
hypothesis, but only after a disagreement between experimental results
was resolved. The "Fifth Force" was a proposed
modification of Newton's Law of Universal Gravitation. The
initial experiments gave conflicting results: one supported the
existence of the Fifth Force whereas the other argued against it.
After numerous repetitions of the experiment, the discord was resolved
and a consensus reached that the Fifth Force did not exist. (For
details of this episode see
 Appendix 4.)


#### 3.3.2 Right Experiment, Wrong Theory: The Stern-Gerlach Experiment



The Stern-Gerlach experiment was regarded as crucial at the time it
was performed, but, in fact,
 wasn't.[12]
 In the view of the physics community it decided the issue between two
theories, refuting one and supporting the other. In the light of later
work, however, the refutation stood, but the confirmation was
questionable. In fact, the experimental result posed problems for the
theory it had seemingly confirmed. A new theory was proposed and
although the Stern-Gerlach result initially also posed problems for
the new theory, after a modification of that new theory, the result
confirmed it. In a sense, it was crucial after all. It just took some
time.



The Stern-Gerlach experiment provides evidence for the existence of
electron spin. These experimental results were first published in
1922, although the idea of electron spin wasn't proposed by
Goudsmit and Uhlenbeck until 1925 (1925; 1926). One might say that
electron spin was discovered before it was invented. (For details of
this episode see
 Appendix 5).


#### 3.3.3 Sometimes Refutation Doesn't Work: The Double-Scattering of Electrons



In the last section we saw some of the difficulty inherent in
experiment-theory comparison. One is sometimes faced with the question
of whether the experimental apparatus satisfies the conditions
required by theory, or conversely, whether the appropriate theory is
being compared to the experimental result. A case in point is the
history of experiments on the double-scattering of electrons by heavy
nuclei (Mott scattering) during the 1930s and the relation of these
results to Dirac's theory of the electron, an episode in which
the question of whether or not the experiment satisfied the conditions
of the theoretical calculation was central. Initially, experiments
disagreed with Mott's calculation, casting doubt on the
underlying Dirac theory. After more than a decade of work, both
experimental and theoretical, it was realized that there was a
background effect in the experiments that masked the predicted effect.
When the background was eliminated experiment and theory agreed.
 (Appendix 6)


#### 3.3.4 The Failure to Detect Anomalies



Ever vaster amounts of data have been produced by particle colliders
as they have grown from room-size apparata, to tens of kilometers long
mega-labs. Vast numbers of background interactions that are well
understood and theoretically uninteresting occur in the detector.
These have to be combed in order to identify interactions of potential
interest. This is especially true of hadron (proton-proton) colliders
like the Large Hadron Collider (LHC), where the Higgs boson was
discovered. Protons that collide in the LHC and similar hadron
colliders are composed of more elementary particles, collectively
labeled partons. Partons mutually interact, exponentially increasing
the number of background interactions. In fact, a minuscule number of
interactions are selected from the overwhelming number that occur in
the detector. (In contrast, lepton collisions, such as collisions of
electrons and positrons, produce much lower backgrounds, since leptons
are not composed of more elementary particles.)



Thus, a successful search for new elementary particles critically
depends on successfully crafting selection criteria and techniques at
the stage of data collection and at the stage of data analysis. But
gradual development and changes in data selection procedures in the
colliders raises an important epistemological concern. The main reason
for this concern is nicely anticipated by the following question,
which was posed by one of the most prominent experimentalists in
particle physics: "What is the extent to which we are negating
the discovery potential of very-high-energy proton machines by the
necessity of rejecting, a priori, the events we cannot afford to
record?" (Panofsky 1994, 133). In other words, how does one
decide which interactions to detect and analyze in a multitude, in
order to minimize the possibility of throwing out novel and unexplored
ones?



One way of searching through vast amounts of data that are already in,
i.e. those that the detector has already delivered, is to look for
occurrences that remain robust under varying conditions of detection.
Physicists employ the technique of data cuts in such analysis. They
cut out data that may be unreliable--when, for instance, a data
set may be an artefact rather than a genuine particle interaction the
experimenters expect. E.g. a colliding beam may interact with the
walls of the detector and not with the other colliding beam, while
producing a signal identical to the signal the experimenters expected
the beam-beam interaction to produce. Thus, if under various data cuts
a result remains stable, then it is increasingly likely to be correct
and to represent the genuine phenomenon the physicists think it
represents. The robustness of the result under various data cuts
minimizes the possibility that the detected phenomenon only mimics the
genuine one (Franklin 2013, 224-5).



At the data-acquisition stage, however, this strategy does not seem
applicable. As Panofsky suggests, one does not know with certainty
which of the vast number of the events in the detector may be of
interest.



Yet, Karaca
 (2011)[13]
 argues that a form of robustness is in play even at the acquisition
stage. This experimental approach amalgamates theoretical expectations
and empirical results, as the example of the hypothesis of specific
heavy particles is supposed to illustrate.



Along with the Standard Model of particle physics, a number of
alternative models have been proposed. Their predictions of how
elementary particles should behave often differ substantially. Yet in
contrast to the Standard Model, they all share the hypothesis that
there exist heavy particles that decay into particles with high
transverse momentum.



Physicists apply a robustness analysis in testing this hypothesis, the
argument goes. First, they check whether the apparatus can detect
known particles similar to those predicted. Second, guided by the
hypothesis, they establish various trigger algorithms. (The trigger
algorithms, or "the triggers", determine at what exact
point in time and under which conditions a detector should record
interactions. They are necessary because the frequency and the number
of interactions far exceed the limited recording capacity.) And,
finally, they observe whether any results remain stable across the
triggers.



Yet even in this theoretical-empirical form of robustness, as Franklin
(2013, 225) points out, "there is an underlying assumption that
any new physics will resemble known physics"--usually a
theory of the day. And one way around this problem is for physicists
to produce as many alternative models as possible, including those
that may even seem implausible at the time.



Perovic (2011) suggests that such a potential failure, namely to spot
potentially relevant events occurring in the detector, may be also a
consequence of the gradual automation of the detection process.



The early days of experimentation in particle physics, around WWII,
saw the direct involvement of the experimenters in the process.
Experimental particle physics was a decentralized discipline where
experimenters running individual labs had full control over the
triggers and analysis. The experimenters could also control the goals
and the design of experiments. Fixed target accelerators, where the
beam hits the detector instead of another beam, produced a number of
particle interactions that was manageable for such labs. The chance of
missing an anomalous event not predicted by the current theory was not
a major concern in such an environment.



Yet such labs could process a comparatively small amount of data. This
has gradually become an obstacle, with the advent of hadron colliders.
They work at ever-higher energies and produce an ever-vaster number of
background interactions. That is why the experimental process has
become increasingly automated and much more indirect. Trained
technicians instead of experimenters themselves at some point started
to scan the recordings. Eventually, these human scanners were replaced
by computers, and a full automation of detection in hadron colliders
has enabled the processing of vast number of interactions. This was
the first significant change in the transition from small individual
labs to mega-labs.



The second significant change concerned the organization and goals of
the labs. The mega-detectors and the amounts of data they produced
required exponentially more staff and scientists. This in turn led to
even more centralized and hierarchical labs and even longer periods of
design and performance of the experiments. As a result, focusing on
confirming existing dominant hypotheses rather than on exploratory
particle searches was the least risky way of achieving results that
would justify unprecedented investments.



Now, an indirect detection process combined with mostly confirmatory
goals is conducive to overlooking of unexpected interactions. As such,
it may impede potentially crucial theoretical advances stemming from
missed interactions.



This possibility that physicists such as Panofsky have acknowledged is
not a mere speculation. In fact, the use of semi-automated, rather
than fully-automated regimes of detection turned out to be essential
for a number of surprising discoveries that led to theoretical
breakthroughs.



Perovic (2011) analyzes several such cases, most notably the discovery
of the J/psi particle that provided the first substantial piece of
evidence for the existence of the charmed quark. In the experiments,
physicists were able to perform exploratory detection and visual
analysis of practically individual interactions due to low number of
background interactions in the linear electron-positron collider. And
they could afford to do this in an energy range that the existing
theory did not recognize as significant, which led to them making the
discovery. None of this could have been done in the fully automated
detecting regime of hadron colliders that are indispensable when
dealing with an environment that contains huge numbers of background
interactions.



And in some cases, such as the Fermilab experiments that aimed to
discover weak neutral currents, an automated and confirmatory regime
of data analysis contributed to the failure to detect particles that
were readily produced in the apparatus.


#### 3.3.5 The 'Look Elsewhere' Effect: Discovering the Higgs Boson



The complexity of the discovery process in particle physics does not
end with concerns about what exact data should be chosen out of the
sea of interactions. The so-called look-elsewhere effect results in a
tantalizing dilemma at the stage of data analysis.



Suppose that our theory tells us that we will find a particle in an
energy range. And suppose we find a significant signal in a section of
that very range. Perhaps we should keep looking elsewhere within the
range to make sure it is not another particle altogether we have
discovered. It may be a particle that left other undetected traces in
the range that our theory does not predict, along with the trace we
found. The question is to what extent we should look elsewhere before
we reach a satisfying level of certainty that it is the predicted
particle we have discovered.



Physicists faced such a dilemma during the search for the Higgs boson
at the Large Hadron Collider at CERN (Dawid 2015).



The Higgs boson is a particle responsible for the mass of other
particles. It is a scalar field that "pulls back" moving
and interacting particles. This pull, which we call mass, is different
for different particles. It is predicted by the Standard Model,
whereas alternative models predict somewhat similar Higgs-like
particles.



A prediction based on the Standard Model tells us with high
probability that we will find the Higgs particle in a particular
range. Yet a simple and an inevitable fact of finding it in a
particular section of that range may prompt us to doubt whether we
have truly found the exact particle our theory predicted. Our initial
excitement may vanish when we realize that we are much more likely to
find a particle of any sort--not just the predicted
particle--within the entire range than in a particular section of
that range. Thus, the probability of finding the Higgs anywhere within
a given energy range (consisting of eighty energy 'bins')
is much higher than the probability of finding it at a particular
energy scale within that range (i.e. in any individual bin). In fact,
the likelihood of us finding it in a particular bin of the range is
about hundred times lower.



In other words, the fact that we will inevitably find the particle in
a particular bin, not only in a particular range, decreases the
certainty that it was the Higgs we found. Given this fact alone we
should keep looking elsewhere for other possible traces in the range
once we find a significant signal in a bin. We should not proclaim the
discovery of a particle predicted by the Standard Model (or any model
for that matter) too soon. But for how long should we keep looking
elsewhere? And what level of certainty do we need to achieve before we
proclaim discovery?



The answer boils down to the weight one gives the theory and its
predictions. This is the reason the experimentalists and theoreticians
had divergent views on the criterion for determining the precise point
at which they could justifiably state 'Our data indicate that we
have discovered the Higgs boson'. Theoreticians were confident
that a finding within the range (any of eighty bins) that was of
standard reliability (of three or four sigma), coupled with the
theoretical expectations that Higgs would be found, would be
sufficient. In contrast, experimentalists argued that at no point of
data analysis should the pertinence of the look-elsewhere effect be
reduced, and the search proclaimed successful, with the help of the
theoretical expectations concerning Higgs. One needs to be as careful
in combing the range as one practically may. As a result, the
experimentalists' preferred value of sigmas for announcing the
discovery was five. This is a standard under which very few findings
have turned out to be a fluctuation in the past.



Dawid argues that a question of an appropriate statistical analysis of
data is at the heart of the dispute. The reasoning of the
experimentalists relied on a frequentist approach that does not
specify the probability of the tested hypothesis. It actually isolates
statistical analysis of data from the prior probabilities. The
theoreticians, however, relied on Bayesian analysis. It starts with
prior probabilities of initial assumptions and ends with the
assessment of the probability of tested hypothesis based on the
collected evidence. The question remains whether the
experimentalists' reasoning was fully justified. The prior
expectations that the theoreticians had included in their analysis had
already been empirically corroborated by previous experiments after
all.


### 3.4 Other Roles


#### 3.4.1 Evidence for a New Entity: J.J. Thomson and the Electron



Experiment can also provide us with evidence for the existence of the
entities involved in our theories. J.J. Thomson's experiments on
cathode rays provided grounds for belief in the existence of
electrons. (For details of this episode see
 Appendix 7).


#### 3.4.2 The Articulation of Theory: Weak Interactions



Experiment can also help to articulate a theory. Experiments on beta
decay during from the 1930s to the 1950s determined the precise
mathematical form of Fermi's theory of beta decay. (For details
of this episode see
 Appendix 8.)


## 4. Experiment and Observation



The distinction between observation and experiment is relatively
little discussed in philosophical literature, despite its continuous
relevance to the scientific community and beyond in understanding
specific traits and segments of the scientific process and the
knowledge it produces.



Daston and her coauthors (Daston 2011; Daston and Lunbeck 2011; Daston
and Galison 2007) have convincingly demonstrated that the distinction
has played a role in delineating various features of scientific
practice. It has helped scientists articulate their reflections on
their own practice.



Observation is philosophically a loaded term, yet the epistemic status
of scientific observation has evolved gradually with the advance of
scientific techniques of inquiry and the scientific communities
pursuing them. Daston succinctly summarizes this evolution in the
following passage:



> 
> Characteristic of the emergent epistemic genre of the observations
> was, first, an emphasis on singular events, witnessed first hand
> (autopsia) by a named author (in contrast to the accumulation of
> anonymous data over centuries described by Cicero and Pliny as typical
> of observationes); second, a deliberate effort to separate observation
> from conjecture (in contrast to the medieval Scholastic connection of
> observation with the conjectural sciences, such as astrology); and
> third, the creation of virtual communities of observers dispersed over
> time and space, who communicated and pooled their observations in
> letters and publications (in contrast to passing them down from father
> to son or teacher to student as rare and precious treasures). (2011,
> 81)
> 



Observation gradually became juxtaposed to other, more complex modes
of inquiry such as experiment, "whose meaning shifted from the
broad and heterogeneous sense of experimentum as recipe, trial, or
just common experience to a concertedly artificial manipulation, often
using special instruments and designed to probe hidden causes"
(Daston 2011, 82).



In the 17th century, observation and experiment were seen as "an
inseparable pair" (Daston 2011, 82) and by the 19th century they
were understood to be essentially opposed, with the observer
increasingly seen as passive and thus epistemically inferior to the
experimenter. In fact, already Leibniz anticipated this view stating
that "[t]here are certain experiments that would be better
called observations, in which one considers rather than produces the
work" (Daston 2011, 86). This aspect of the distinction has been
a mainstay of understanding scientific practice ever since.



Shapere (1982) pointed out that the usage of the notion of observation
is embedded in scientific practice, including testing and
justification of scientific theories. Neutrinos arriving from the Sun
are said to be observed in the detector but are also said to be an
observation of the Sun's core. Yet, the background knowledge
provides the foundation for a meaningful distinction. One the one hand
there are weakly interacting neutrinos leaving the Sun's core
and entering detector practically interrupted. This may be justifiably
qualified as "direct observation" of the Sun's core.
On the other hand, there is a rather indirect observation of the core
via detection of light-photons that travel for billions of years from
the Sun's core through the plasma to the electromagnetic
detectors.



There are currently two prominent and opposed views of the
experiment-observation distinction. Ian Hacking has characterized it
as well-defined, while avoiding the claim that observation and
experiment are opposites (Hacking 1983, 173). According to him, the
notions signify different things in scientific practice. The
experiment is a thorough manipulation that creates a new phenomenon,
and observation of the phenomenon is its outcome. If scientists can
manipulate a domain of nature to such an extent that they can create a
new phenomenon in a lab, a phenomenon that normally cannot be observed
in nature, then they have truly observed the phenomenon (Hacking 1989,
1992).



Meanwhile, other authors concur that "the familiar distinction
between observation and experiment ... [is] an artefact of the
disembodied, reconstructed character of retrospective accounts"
(Gooding 1992, 68). The distinction "collapses" when we
are faced with actual scientific practice as a process, and
"Hacking's observation versus experiment framework does
not survive intact when put to the test in a range of cases of
scientific experimentation" (Malik 2017, 85). First, the uses of
the distinction cannot be compared across scientific fields. And
second, as Gooding (1992) suggests, observation is a process too, not
simply a static result of manipulation. Thus, both observation and
experiment are seen as concurrent processes blended together in
scientific practice.



Malik (2017, 86) states that these arguments are the reason why
"very few [authors] use Hacking's nomenclature of
observation/experiment" and goes so far to conclude that
"to (try to) distinguish between observation and experiment is
futile." There is no point delineating the two except perhaps in
certain narrow domains; e.g., Hacking's notion of the experiment
based on creating phenomena might be useful within a narrow domain of
particle physics. (See also Chang 2011.) He advocates avoiding the
distinction altogether and opting for "the terminology [that]
underlines this sense of continuousness" (Malik 2017, 88)
instead. If we want to analyze scientific practice, the argument goes,
we should leave behind the idea of the distinction as fundamental and
turn to the characterization and analysis of various "epistemic
activities" instead, e.g., along the lines suggested by Chang
(2011).



A rather obvious danger of this approach is an over-emphasis on the
continuousness of the notions of observation and experiment that
results in inadvertent equivocation. And this, in turn, results in
sidelining the distinction and its subtleties in the analysis of the
scientific practice, despite their crucial role in articulating and
developing that practice since the 17th century. It is possible
that these two notions form a continuum spreading along the axes of
manipulability and accessibility of both target phenomena and
observational conditions, and that the key points on such continuum
define various evolving practices. Thus, each scientific practice may
be located on the continuum, with the location defining both its
epistemic properties and the epistemic (as well as ethical)
obligations that underlie it at a given time. (Perovic 2021)



On the one hand, the extent of the manipulation of phenomena and
research conditions ranges from bodily manipulations (e.g.
finding a convenient location to observe a planet with the naked eye)
to the production of new phenomena in an elaborate apparatus like LHC
at CERN, where the label "experiment" aims to delineate a
substantial threshold of manipulation. On the other hand, depending on
the background knowledge and aims of the research, observational
accessibility ranges from mere detection of a potentially interesting
phenomenon (e.g. a metal detector detects something in the ground),
all the way to direct observation of the phenomenon's properties
(e.g., the microscopic analysis of a metal object).


## 5. Some Comparisons With Experiment in Biology


### 5.1 Epistemological Strategies and the Peppered Moth Experiment



One comment that has been made concerning the philosophy of experiment
is that all of the examples are taken from physics and are therefore
limited. In this section arguments will be presented that these
discussions also apply to biology.



Although all of the illustrations of the epistemology of experiment
come from physics, David Rudge (1998; 2001) has shown that they are
also used in biology. His example is Kettlewell's (1955; 1956;
1958) evolutionary biology experiments on the Peppered Moth,
*Biston betularia*. The *typical* form of the moth has a
pale speckled appearance and there are two darker forms, f.
*carbonaria*, which is nearly black, and f. *insularia*,
which is intermediate in color. The *typical* form of the moth
was most prevalent in the British Isles and Europe until the middle of
the nineteenth century. At that time things began to change.
Increasing industrial pollution had both darkened the surfaces of
trees and rocks and had also killed the lichen cover of the forests
downwind of pollution sources. Coincident with these changes,
naturalists had found that rare, darker forms of several moth species,
in particular the Peppered Moth, had become common in areas downwind
of pollution sources.



Kettlewell attempted to test a selectionist explanation of this
phenomenon. E.B. Ford (1937; 1940) had suggested a two-part
explanation of this effect: 1) darker moths had a superior physiology
and 2) the spread of the melanic gene was confined to industrial areas
because the darker color made *carbonaria* more conspicuous to
avian predators in rural areas and less conspicuous in polluted areas.
Kettlewell believed that Ford had established the superior viability
of darker moths and he wanted to test the hypothesis that the darker
form of the moth was less conspicuous to predators in industrial
areas.



Kettlewell's investigations consisted of three parts. In the
first part he used human observers to investigate whether his proposed
scoring method would be accurate in assessing the relative
conspicuousness of different types of moths against different
backgrounds. The tests showed that moths on "correct"
backgrounds, *typical* on lichen covered backgrounds and dark
moths on soot-blackened backgrounds were almost always judged
inconspicuous, whereas moths on "incorrect" backgrounds
were judged conspicuous.



The second step involved releasing birds into a cage containing all
three types of moth and both soot-blackened and lichen covered pieces
of bark as resting places. After some difficulties (see Rudge 1998 for
details), Kettlewell found that birds prey on moths in an order of
conspicuousness similar to that gauged by human observers.



The third step was to investigate whether birds preferentially prey on
conspicuous moths in the wild. Kettlewell used a
mark-release-recapture experiment in both a polluted environment
(Birmingham) and later in an unpolluted wood. He released 630 marked
male moths of all three types in an area near Birmingham, which
contained predators and natural boundaries. He then recaptured the
moths using two different types of trap, each containing virgin
females of all three types to guard against the possibility of
pheromone differences.



Kettlewell found that *carbonaria* was twice as likely to
survive in soot-darkened environments (27.5 percent) as was
*typical* (12.7 percent). He worried, however, that his results
might be an artifact of his experimental procedures. Perhaps the traps
used were more attractive to one type of moth, that one form of moth
was more likely to migrate, or that one type of moth just lived
longer. He eliminated the first alternative by showing that the
recapture rates were the same for both types of trap. The use of
natural boundaries and traps placed beyond those boundaries eliminated
the second, and previous experiments had shown no differences in
longevity. Further experiments in polluted environments confirmed that
*carbonaria* was twice as likely to survive as
*typical.* An experiment in an unpolluted environment showed
that *typical* was three times as likely to survive as
*carbonaria*. Kettlewell concluded that such selection was the
cause of the prevalence of *carbonaria* in polluted
environments.



Rudge also demonstrates that the strategies used by Kettlewell are
those described above in the epistemology of experiment. His examples
are given in Table 1. (For more details see Rudge 1998).





|  |  |  |
| --- | --- | --- |
|  | **Epistemological strategies** | **Examples from Kettlewell** |
| 1. | Experimental checks and calibration in which the apparatus
reproduces known phenomena. | Use of the scoring experiment to verify that the proposed
scoring methods would be feasible and objective. |
| 2. | Reproducing artifacts that are known in advance to be
present. | Analysis of recapture figures for endemic *betularia*
populations. |
| 3. | Elimination of plausible sources of background and alternative
explanations of the result. | Use of natural barriers to minimize migration. |
| 4. | Using the results themselves to argue for their validity. | Filming the birds preying on the moths. |
| 5. | Using an independently well-corroborated theory of the
phenomenon to explain the results. | Use of Ford's theory of the spread of industrial
melanism. |
| 6. | Using an apparatus based on a well- corroborated theory. | Use of Fisher, Ford, and Shepard techniques. [The
mark-release-capture method had been used in several earlier
experiments] |
| 7. | Using statistical arguments. | Use and analysis of large numbers of moths. |
| 8. | Blind analysis | Not used. |
| 9. | Intervention, in which the experimenter manipulates the object
under observation | Not present |
| 10. | Independent confirmation using different experiments. | Use of two different types of traps to recapture the moths. |



Table 1. Examples of epistemological
strategies used by experimentalists in evolutionary biology, from
H.B.D. Kettlewell's (1955, 1956, 1958) investigations of
industrial melanism. (See Rudge 1998).



### 5.2 The Meselson-Stahl Experiment: "The Most Beautiful Experiment in Biology"



The roles that experiment plays in physics are also those it plays in
biology. In the previous section we have seen that Kettlewell's
experiments both test and confirm a theory. I discussed earlier a set
of crucial experiments that decided between two competing classes of
theories, those that conserved parity and those that did not. In this
section I will discuss an experiment that decided among three
competing mechanisms for the replication of DNA, the molecule now
believed to be responsible for heredity. This is another crucial
experiment. It strongly supported one proposed mechanism and argued
against the other two. (For details of this episode see Holmes
2001.)



In 1953 Francis Crick and James Watson proposed a three-dimensional
structure for deoxyribonucleic acid (DNA) (Watson and Crick 1953a).
Their proposed structure consisted of two polynucleotide chains
helically wound about a common axis. This was the famous "Double
Helix". The chains were bound together by combinations of four
nitrogen bases -- adenine, thymine, cytosine, and guanine.
Because of structural requirements only the base pairs adenine-thymine
and cytosine-guanine are allowed. Each chain is thus complementary to
the other. If there is an adenine base at a location in one chain
there is a thymine base at the same location on the other chain, and
vice versa. The same applies to cytosine and guanine. The order of the
bases along a chain is not, however, restricted in any way, and it is
the precise sequence of bases that carries the genetic
information.



The significance of the proposed structure was not lost on Watson and
Crick when they made their suggestion. They remarked, "It has
not escaped our notice that the specific pairing we have postulated
immediately suggests a possible copying mechanism for the genetic
material."



If DNA was to play this crucial role in genetics, then there must be a
mechanism for the replication of the molecule. Within a short period
of time following the Watson-Crick suggestion, three different
mechanisms for the replication of the DNA molecule were proposed
(Delbruck and Stent 1957). These are illustrated in Figure A. The
first, proposed by Gunther Stent and known as conservative
replication, suggested that each of the two strands of the parent DNA
molecule is replicated in new material. This yields a first generation
which consists of the original parent DNA molecule and one
newly-synthesized DNA molecule. The second generation will consist of
the parental DNA and three new DNAs.



![Possible mechanisms for DNA replication](figA.jpg)

Figure A: Possible mechanisms for DNA
replication. (Left) Conservative replication. Each of the two strands
of the parent DNA is replicated to yield the unchanged parent DNA and
one newly synthesized DNA. The second generation consists of one
parent DNA and three new DNAs. (Center) Semiconservative replication.
Each first generation DNA molecule contains one strand of the parent
DNA and one newly synthesized strand. The second generation consists
of two hybrid DNAs and two new DNAs. (Right) Dispersive replication.
The parent chains break at intervals, and the parental segments
combine with new segments to form the daughter chains. The darker
segments are parental DNA and the lighter segments are newly
synthesized DNA. From Lehninger (1975).




The second proposed mechanism, known as semiconservative replication
is when each strand of the parental DNA acts as a template for a
second newly-synthesized complementary strand, which then combines
with the original strand to form a DNA molecule. This was proposed by
Watson and Crick (1953b). The first generation consists of two hybrid
molecules, each of which contains one strand of parental DNA and one
newly synthesized strand. The second generation consists of two hybrid
molecules and two totally new DNAs. The third mechanism, proposed by
Max Delbruck, was dispersive replication, in which the parental DNA
chains break at intervals and the parental segments combine with new
segments to form the daughter strands.



In this section the experiment performed by Matthew Meselson and
Franklin Stahl, which has been called "the most beautiful
experiment in biology", and which was designed to answer the
question of the correct DNA replication mechanism will be discussed
(Meselson and Stahl 1958). Meselson and Stahl described their proposed
method. "We anticipated that a label which imparts to the DNA
molecule an increased density might permit an analysis of this
distribution by sedimentation techniques. To this end a method was
developed for the detection of small density differences among
macromolecules. By use of this method, we have observed the
distribution of the heavy nitrogen isotope \(\ce{^{15}N}\) among
molecules of DNA following the transfer of a uniformly
\(\ce{^{15}N}\)-labeled, exponentially growing bacterial population to
a growth medium containing the ordinary nitrogen isotope
\(\ce{^{14}N}\)" (Meselson and Stahl 1958, pp.
671-672).



![Meselson-Stahl schematic](figB.jpg)

Figure B: Schematic representation of
the Meselson-Stahl experiment. From Watson (1965).




The experiment is described schematically in Figure B. Meselson and
Stahl placed a sample of DNA in a solution of cesium chloride. As the
sample is rotated at high speed the denser material travels further
away from the axis of rotation than does the less dense material. This
results in a solution of cesium chloride that has increasing density
as one goes further away from the axis of rotation. The DNA reaches
equilibrium at the position where its density equals that of the
solution. Meselson and Stahl grew *E. coli* bacteria in a
medium that contained ammonium chloride \((\ce{NH4Cl})\) as the sole
source of nitrogen. They did this for media that contained either
\(\ce{^{14}N}\), ordinary nitrogen, or \(\ce{^{15}N}\), a heavier
isotope. By destroying the cell membranes they could obtain samples of
DNA which contained either \(\ce{^{14}N}\) or \(\ce{^{15}N}\). They
first showed that they could indeed separate the two different mass
molecules of DNA by centrifugation (Figure C). The separation of the
two types of DNA is clear in both the photograph obtained by absorbing
ultraviolet light and in the graph showing the intensity of the
signal, obtained with a densitometer. In addition, the separation
between the two peaks suggested that they would be able to distinguish
an intermediate band composed of hybrid DNA from the heavy and light
bands. These early results argued both that the experimental apparatus
was working properly and that all of the results obtained were
correct. It is difficult to imagine either an apparatus malfunction or
a source of experimental background that could reproduce those
results. This is similar, although certainly not identical, to
Galileo's observation of the moons of Jupiter or to
Millikan's measurement of the charge of the electron. In both of
those episodes it was the results themselves that argued for their
correctness.



![Meselson-Stahl schematic](figC.jpg)

Figure C: The separation of
\(\ce{^{14}N}\) DNA from \(\ce{^{15}N}\) DNA by centrifugation. The
band on the left is \(\ce{^{14}N}\) DNA and that on the right is from
\(\ce{^{15}N}\) DNA. From Meselson and Stahl (1958).




Meselson and Stahl then produced a sample of *E coli* bacteria
containing only \(\ce{^{15}N}\) by growing it in a medium containing
only ammonium chloride with \(\ce{^{15}N}\) \((\ce{^{15}NH4Cl})\) for
fourteen generations. They then abruptly changed the medium to
\(\ce{^{14}N}\) by adding a tenfold excess of \(\ce{^{14}NH\_4Cl}\).
Samples were taken just before the addition of \(\ce{^{14}N}\) and at
intervals afterward for several generations. The cell membranes were
broken to release the DNA into the solution and the samples were
centrifuged and ultraviolet absorption photographs taken. In addition,
the photographs were scanned with a recording densitometer. The
results are shown in Figure D, showing both the photographs and the
densitometer traces. The figure shows that one starts only with heavy
(fully-labeled) DNA. As time proceeds one sees more and more
half-labeled DNA, until at one generation time only half-labeled DNA
is present. "Subsequently only half labeled DNA and completely
unlabeled DNA are found. When two generation times have elapsed after
the addition of \(\ce{^{14}N}\) half-labeled and unlabeled DNA are
present in equal amounts" (p. 676). (This is exactly what the
semiconservative replication mechanism predicts). By four generations
the sample consists almost entirely of unlabeled DNA. A test of the
conclusion that the DNA in the intermediate density band was half
labeled was provided by examination of a sample containing equal
amounts of generations 0 and 1.9. If the semiconservative mechanism is
correct then Generation 1.9 should have approximately equal amounts of
unlabeled and half-labeled DNA, whereas Generation 0 contains only
fully-labeled DNA. As one can see, there are three clear density bands
and Meselson and Stahl found that the intermediate band was centered
at \((50 \pm 2)\) percent of the difference between the
\(\ce{^{14}N}\) and \(\ce{^{15}N}\) bands, shown in the bottom
photograph (Generations 0 and 4.1). This is precisely what one would
expect if that DNA were half labeled.



![Absorption photographs and densitometer traces](figD.jpg)

Figure D: (Left) Ultraviolet absorption
photographs showing DNA bands from centrifugation of DNA from *E.
Coli* sampled at various times after the addition of an excess of
\(\ce{^{14}N}\) substrates to a growing \(\ce{^{15}N}\) culture.
(Right) Densitometer traces of the photographs. The initial sample is
all heavy (\(\ce{^{15}N}\) DNA). As time proceeds a second
intermediate band begins to appear until at one generation all of the
sample is of intermediate mass (Hybrid DNA). At longer times a band of
light DNA appears, until at 4.1 generations the sample is almost all
lighter DNA. This is exactly what is predicted by the Watson-Crick
semiconservative mechanism. From Meselson and Stahl (1958)




Meselson and Stahl stated their results as follows, "The
nitrogen of DNA is divided equally between two subunits which remain
intact through many generations.... Following replication, each
daughter molecule has received one parental subunit" (p.
676).



Meselson and Stahl also noted the implications of their work for
deciding among the proposed mechanisms for DNA replication. In a
section labeled "The Watson-Crick Model" they noted that,
"This [the structure of the DNA molecule] suggested to Watson
and Crick a definite and structurally plausible hypothesis for the
duplication of the DNA molecule. According to this idea, the two
chains separate, exposing the hydrogen-bonding sites of the bases.
Then, in accord with base-pairing restrictions, each chain serves as a
template for the synthesis of its complement. Accordingly, each
daughter molecule contains one of the parental chains paired with a
newly synthesized chain.... The results of the present experiment
are in exact accord with the expectations of the Watson-Crick model
for DNA replication" (pp. 677-678).



It also showed that the dispersive replication mechanism proposed by
Delbruck, which had smaller subunits, was incorrect. "Since the
apparent molecular weight of the subunits so obtained is found to be
close to half that of the intact molecule, it may be further concluded
that the subunits of the DNA molecule which are conserved at
duplication are single, continuous structures. The scheme for DNA
duplication proposed by Delbruck is thereby ruled out" (p. 681).
Later work by John Cairns and others showed that the subunits of DNA
were the entire single polynucleotide chains of the Watson-Crick model
of DNA structure.



The Meselson-Stahl experiment is a crucial experiment in biology. It
decided between three proposed mechanisms for the replication of DNA.
It supported the Watson-Crick semiconservative mechanism and
eliminated the conservative and dispersive mechanisms. It played a
similar role in biology to that of the experiments that demonstrated
the nonconservation of parity did in physics. Thus, we have seen
evidence that experiment plays similar roles in both biology and
physics and also that the same epistemological strategies are used in
both disciplines.


## 6. Computer Simulations and Experimentation



One interesting recent development in science, and thus in the
philosophy of science, has been the increasing use of, and importance
of, computer simulations. In some fields, such as high-energy physics,
simulations are an essential part of all experiments. It is fair to
say that without computer simulations these experiments would be
impossible. There has been a considerable literature in the philosophy
of science discussing whether computer simulations are experiments,
theory, or some new kind of hybrid method of doing science. But, as
Eric Winsberg remarked, "We have in other words, rejected the
overly conservative intuition that computer simulation is nothing but
boring and straightforward theory application. But we have avoided
embracing the opposite, overly grandiose intuition that simulation is
a radically new kind of knowledge production, "on a par"
with experimentation. In fact, we have seen that soberly locating
simulation "on the methodological map" is not a simple
matter (Winsberg 2010, p. 136)."



Given the importance of computer simulations in science it is
essential that we have good reasons to believe their results. Eric
Winsberg (2010), Wendy Parker (2008) and others have shown that
scientists use strategies quite similar to those discussed in Section
1.1.1, to argue for the correctness of computer simulations.


## 7. Conclusion



In this entry varying views on the nature of experimental results have
been presented. Some argue that the acceptance of experimental results
is based on epistemological arguments, whereas others base acceptance
on future utility, social interests, or agreement with existing
community commitments. Everyone agrees , however, that for whatever
reasons, a consensus is reached on experimental results. These results
then play many important roles in physics and we have examined several
of these roles, although certainly not all of them. We have seen
experiment deciding between two competing theories, calling for a new
theory, confirming a theory, refuting a theory, providing evidence
that determined the mathematical form of a theory, and providing
evidence for the existence of an elementary particle involved in an
accepted theory. We have also seen that experiment has a life of its
own, independent of theory. If, as I believe, epistemological
procedures provide grounds for reasonable belief in experimental
results, then experiment can legitimately play the roles I have
discussed and can provide the basis for scientific knowledge.