## 1. Experimentation and Causal Reasoning


### 1.1 Mill's Methods in Experimental Biology



Causal reasoning approaches try to reconstruct and sometimes justify
the rules that allow scientists to infer causal relationships from
data, including experimental data. One of the oldest such attempts is
due to John Stuart Mill (1996 [1843]), who presented a systematic
account of causal inference that consisted of five different so-called
"methods": The Method of Agreement, the Method of
Difference, the Joint Method of Agreement and of Difference, the
Method of Residues, and the Method Concomitant Variation. While some
of these "methods" pertain more to observation, the Method
of Difference in particular is widely seen as encapsulating an
important principle of scientific reasoning based on experiment. Mill
himself characterized it thus: "If an instance in which the
phenomenon under investigation occurs, and an instance in which it
does not occur, have every circumstance in common save one, that one
occurring only in the former; the circumstance in which alone the two
instances differ, is the effect, or the cause, or an indispensable
part of the cause, of the phenomenon" (Mill 1996 [1843], Ch. 8,
SS2). Thus, Mill's method of difference asks us to look at two
situations: one in which the phenomenon under investigation occurs,
and one in which it does not occur. If a factor can be identified that
is the only other difference between the two situations, then this
factor must be causally relevant.



As Mill noted, the method of difference is particularly germane to
experimental inquiry because such a difference as is required by this
method can often be produced by an experimental intervention. Indeed,
according to a position known as interventionism about causality there
is a tight connection between the concept of cause and experimental
interventions (Woodward 2003).



Mill's method of difference captures an important kind of reasoning
that is used frequently in biological experiments. Let's suppose we
want to find out if a newly discovered compound is an antibiotic,
i.e., inhibits the growth of certain bacteria. We start by dividing a
bacterial cell culture into several aliquots (samples of same size
derived from a homogeneous solution). Then, we add to one group of
aliquots the suspected antibiotic that is dissolved in phosphate
buffer ("treatment"). To the other group, we add only the
phosphate buffer ("control"). Then we record bacterial
growth in all the samples (e.g., by measuring the increase in optical
density as the culture medium clouds up due to the bacteria). This
experimental setup makes sure that the treatment and control samples
differ only in the presence or absence of the antibiotic, thus ruling
out that any observed difference in growth between the treatment and
control aliquots is caused not by the suspected antibiotic but by the
buffer solution. Let us denote the antibiotic as "A" and
the growth inhibition as "W". Biologists would thus infer
from this experiment that A is an antibiotic if W is observed in the
samples containing A but not in the samples not containing A.



Mill construed this "method" in terms of a principle of
*inductive* inference that can be justified pragmatically.
However, it is interesting to note that the principle can also be
viewed as instantiating a form of *deductive* inference.



To this end, of course, the Method of Difference must be strengthened
with additional premises. Here is one way how this can be done
(adapted from Hofmann and Baumgartner 2011):


1. S1 and S2 are two homogeneous test
situations (assumption)
2. Two factors A and W both occur in S1 both not in
S2 (exp. result)
3. W is an effect in a deterministic causal structure
(assumption)
4. In S1 there exists a cause of the occurrence of W (from
2, 3)
5. In S2 there exists no cause of the occurrence of W
(from 2,3)
6. S2 contains no confounder of W (from 5)
7. S1 contains no confounder of W (from 1,6)
8. The cause of W belongs to the set {A, W} (from 4, 7)
9. W does not cause itself (assumption)
10. A is the cause or a part of the cause existing in
S1



Some of the terms used in this deduction require explication. Two test
situations are *homogeneous* on the condition that, if a factor
is causally relevant and is present in test situation S1,
then it is also present in test situation S2, and vice
versa. A *confounder* would be a causally relevant factor that
does not belong to the set {A, W}. The presence of such a confounder
is excluded by the assumption of causal homogeneity (1). In practical
situations, a confounder might be an unknown or uncontrolled (i.e.,
not measurable or not measured) factor that is present in only one of
the test situations. In our antibiotics example, this could be some
chemical that was put into just one aliquot inadvertently or without
knowledge of the experimenter. In fact, the risk of a confounder is
precisely why our biological experimenter will divide up the mother
culture into aliquots just before putting in the substance to be
tested. This makes it unlikely that one aliquot contains an
uncontrolled chemical that the other does not contain. Furthermore, a
skilled experimenter will make sure that the cultures are well
stirred, thus preventing a physical-chemical inhomogeneity of the
culture (e.g., some chemical or temperature gradient). Thus, there are
typical laboratory manipulations and procedures that reduce the risk
of confounders.



In spite of these control procedures, it is clear that the derivation
of a causal factor from a Millean difference test presupposes strong
assumptions. In particular, it must be assumed that we are dealing
with a deterministic causal structure (3) and that nothing happens
uncaused (4). In our simple example, this amounts to assuming that the
bacteria don't exhibit any kind of spontaneity, in other words, their
growth behavior is assumed to be determined by their genetic
constitution and their environment (although most biologists are
convinced that their experimental organisms have good and bad days
just like themselves!).



If we thus construe Millean causal reasoning as deductive reasoning,
all the inferential risks are shifted from the induction rules into
the premises such as causal homogeneity, determinism and the principle
of universal causality. It is a characteristic feature of inductive
inference that this is always possible (Norton 2003). A justification
of these premises, of course, does not exist. They may be viewed as
being part and parcel of a certain kind of experimental practice that
is vindicated as a whole by its fruitfulness for research (see
 Section 5).


### 1.2 Generalizations of Mill's Methods



Mill's methods can be formalized and generalized into rich and
sophisticated methodologies of causal reasoning (e.g., Ragin 1987,
Baumgartner 2009, Grasshoff 2011, Beirlaen, Leuridan and Van De
Putte 2018). Such accounts haven been successfully used in the
reconstruction of historical episodes such as the discovery of the
urea cycle (Grasshoff, Casties and Nickelsen 2000; Grasshoff and
May 1995).



Mill's methods and their generalized versions may even be viewed as
providing some kind of a logic of discovery (see also Schaffner 1974),
the existence of which has long been controversial (Nickles 1980).
However, it should be noted that the methods of causal reasoning do
not generate causal knowledge from scratch, as it were. They already
take causal hypotheses as inputs and refine them in an iterative way
(Grasshoff 2011). While some formulations (including Mill's own
mentioned above) may suggest that the inputs to Mill's methods are
mere associations or regularities, it should be clear by now that the
method is only reliable if some kind of causal knowledge is already at
hand. In our example above, the causal assumption is that of causal
homogeneity, which obviously has causal content. This vindicates the
slogan "no causes in, no causes out" (Cartwright 1989, Ch.
2).



This discussion has focused on deterministic causal reasoning, which
is widespread in experimental biology. It should be mentioned that, of
course, there are also statistical inference methods of the kind
formalized in Spirtes, Glymour and Scheines (2000) in use, in
particular regression analysis and analysis of variance, which are
frequently used in biological field experiments. Wet lab experiments,
by contrast, rarely require such techniques.



Some enthusiasts of causal inference methods believe that a
sophisticated version of Mill's methods (and their statistical
counterparts) are basically all that is needed in order to account for
experimental practice (e.g., Grasshoff 2011). An attraction of
this view is that it can be construed essentially as requiring only
deduction and no cumbersome inductive methods.


### 1.3 Mechanistic Constitution and Interlevel Experiments



Experimental methodology has traditionally been mainly concerned with
inferring causal dependencies. However, recent research suggests that
we need to broaden its scope. A considerable body of scholarship
documents that much biological research is best described in terms of
the search for mechanisms, which may be understood as collections of
entities and activities that produce a phenomenon that biologists want
to understand (e.g., Wimsatt 1974, Machamer, Darden and Craver 2000,
Glennan 2005, Bechtel 2006, Craver 2007a). Mechanisms are both what
biological science is aiming at and a means to this end, for sketches
or schemes of mechanisms can guide scientists in the discovery of
missing parts (Darden and Craver 2002, Scholl and Nickelsen 2015).



According to Craver (2007b), we should distinguish between two kinds
of relations that make up mechanisms: (1) causal and (2) constitutive
relations. The former may hold between different parts of a mechanism.
For example, in the basic mechanism of synaptic transmission at the
terminal part of a neuron, the influx of calcium causes the release of
neurotransmitter in the space between the synaptic terminal and the
postsynaptic cell membrane. This causal link can be understood pretty
much as discussed in the last two sections. The other kind of
relation, mechanistic constitutive relevance (or just mechanistic
constitution) holds between the parts and of a mechanism and the
phenomenon the mechanism is for. For example, the influx of calcium
into an axon terminal, together with other events, constitutes the
phenomenon of synaptic transmission. Craver (2007b) contends that this
is not a causal relation because the relata cannot be viewed as
distinct and non-overlapping.



But what defines constitutive relevance? Inspired by interventionism
about causality, Craver argued that it is best defined by the kinds of
interventions that are used by biologists in order to find out whether
some entity and an associated activity are part of a mechanism: by
certain kinds of experiments. In particular, there are two kinds of
so-called interlevel experiments the combination of which establishes
(and defines) constitutive relevance. In the first kind, an
intervention is performed on some part and an ensuing change is
observed in the phenomenon under study. To return to our synaptic
example, a calcium antagonist may be used to show that preventing the
binding of calcium ions to their receptors prevents the release of
neurotransmitter. This is a bottom-up experiment. The second kind of
inter-level experiment intervenes on the phenomenon as a whole in
order to see some change in the parts. For example, stimulating
synaptic transmission by increasing the rate by which action
potentials arrive at the terminal will lead to a measurable increase
in calcium influx at this terminal. This can be done, for example, by
asking a subject to perform a cognitive task (such as trying to
memorize something) and by observing changes in calcium concentration
by functional magnetic resonance imaging (fMRI). Thus, mechanistic
constitution is defined by the mutual manipulability of the parts of
mechanisms and the mechanism as a whole.



Recent debate has challenged the mutual manipulability account
(Leuridan 2012, Harinen 2018, Romero 2015). One issue is that
inter-level experiments are necessarily "fat-handed"
(Baumgartner and Gebharter 2016) because they change the values of at
least two different variables residing at different levels (e.g.,
calcium binding and synaptic transmission, where the former is a part
of the latter). But this threatens to undermine the inferences to
mechanistic constitution. A possible solution might consist in
inferring constituents abductively, by positing constitutive relations
as the best explanation for the presence of common causes that
unbreakably correlate phenomena and their constituents (Baumgartner
and Casini 2017).



Thus, the discovery of mechanisms in biology may require a set of
experimental reasoning principles that must supplement Mill's
methods, even if there are considerable similarities between these
principles and the better-known principles of causal inference
(Harbecke 2015).


## 2. Crucial Experimental Evidence


### 2.1 Duhem's Predicament and the Oxidative Phosphorylation Controversy



Biological textbooks are replete with famous experiments that are
presented as having provided crucial experimental evidence for some
hypothesis. To name just a few examples: Oswald Avery, Colin MacLeod
and Maclyn McCarthy (1944) are reputed to have established DNA as the
carrier of hereditary information by a set of ingenious transformation
experiments using a bacterium causing lung infection,
*Pneumococcus*. Matthew Meselson and Frank Stahl (1958)
conducted an experiment in that is widely thought to have provided
evidence that DNA replication is semi-conservative rather than
conservative or dissipative (meaning that a newly formed DNA double
helix contains one intact strand from the parent molecule and one
newly synthesized strand). Ephraim Racker and Walter Stoeckenius
(1974) are thought to have provided experimental evidence that settled
the long-standing controversy (known as the "oxidative
phosphorylation or ox-phos controversy") as to whether
respiration and the generation of the energy-rich compound ATP in
mitochondria are coupled through a chemical intermediate or a proton
gradient.



Many philosophers of science have been skeptical about the possibility
of such "crucial experiments". Most famous are the
arguments provided by Pierre Duhem (1905), who claimed that crucial
experimental are impossible (in physics) because, even if they succeed
in eliminating a false hypothesis, this does not prove that the
remaining hypothesis is true. Scientists, unlike mathematicians, are
never in possession of a complete set of hypotheses one of which must
be true. It is always possible that the true hypothesis has not yet
been conceived, thus eliminating all but one hypothesis by crucial
experiments will not necessarily lead to the truth.



Based on such considerations, it could be argued that the function of
the alleged crucial experiments in biological textbooks is more
pedagogical than evidential. In order to assess this claim, I will
consider two examples in somewhat greater detail, namely the ox-phos
controversy and the Meselson-Stahl case.



The ox-phos controversy was about the mechanism by which respiration
(i.e., the oxidation of energy-rich compounds) is coupled to the
phosphorylation of ADP (adenosine diphosphate) to ATP (adenosine
triphosphate). The reverse reaction, hydrolysis of ATP to ADP and
inorganic phosphate, is used by cells to power numerous biochemical
reactions such as the synthesis of proteins as well as small
molecules, the replication of DNA, locomotion, and many more (the
energy for muscle contraction is also provided by ATP hydrolysis).
Thus, ATP functions like a universal biochemical battery that is used
to power all kinds of cellular processes. So how can the cell use the
chemical energy contained in food to charge these batteries? A first
pathway that generates ATP from ADP to be described was glycolysis,
the degradation of sugar. This pathway does not require oxygen. The
way it works is that the breakdown of sugar is used by the cell to
make an activated phosphate compound - a so-called high-energy
intermediate - that subsequently transfers its phosphate group
to ADP to make ATP. 



It was clear already in the 1940s that this cannot be the only process
that makes ATP, as it is anaerobic (doesn't require oxygen) and not
very efficient. The complete breakdown of food molecules requires
oxygen. Hans Krebs showed that this occurs in a cyclic reaction
pathway today known as the Krebs cycle. The Krebs cycle generates a
compound called reduced NADH (nicotinamide adenine dinucleotide). The
big question in biochemistry from the 1940s onward was how this
compound was oxidized and how this oxidation was coupled to the
phosphorylation of ADP. Naturally, biochemists searched for a
high-energy intermediate as it was used in glycolysis. However, this
intermediate proved to be extremely elusive.



In 1961, the British biochemist Peter Mitchell (1961) suggested a
mechanism for oxidative phosphorylation (as this process became known)
that did not require a high-energy intermediate. According to
Mitchell's scheme, NADH is oxidized step-wise on the inner membranes
of mitochondria (membrane-bounded intracellular organelles that are
canonically described as the cell's power stations). This process
occurs asymmetrically with respect to the membrane such that a net
transport of protons across the membrane occurs (later it was shown
that the protons are actually transported across proteinaceous pores
in the membrane). Thus, a concentration gradient of protons builds up.
As protons are electrically charged, this gradient also creates a
voltage difference across the membrane. How is this energy used?
According to Mitchell, the membrane contains another enzyme that uses
the energy of the proton gradient to directly phosphorylate ADP. Thus,
it is the proton gradient that couples the reduction of NADH to the
phosphorylation of ADP, not a chemical high-energy intermediate. This
mechanism became known as the "chemi-osmotic mechanism".



Mitchell's hypothesis was met with considerable skepticism, in spite
of the fact that Mitchell and a co-worker were quickly able to produce
experimental evidence in its favor. Specifically, he was able to
demonstrate that isolated respiring mitochondria indeed expel protons
(thus leading to a detectable acidification of the surrounding
solution), as his hypothesis predicted. However, this evidence was
dismissed by most of the biochemists at that time as inconclusive. For
it was difficult to rule out at that time that the proton expulsion by
respiring mitochondria was a mere side-effect of respiration, while
the energy coupling was still mediated by a chemical intermediate.



This was the beginning of one of the most epic controversies in the
history of 20th Century biochemistry. It took the larger part of a
decade to resolve this issue, time during which several laboratories
claimed success in finding the elusive chemical intermediate. But none
of these findings survived critical scrutiny. On the other side, all
the evidence adduced by Mitchell and his few supporters was considered
non-conclusive for the reasons mentioned above. Weber (2002) shows
that the two competing theories of oxidative phosphorylation can be
viewed as incommensurable in the sense of T.S. Kuhn (1970), without
thereby being incomparable (as Kuhn is often misread).



Nonetheless, the controversy was eventually closed in the mid-1970s in
Mitchell's favor, earning him the 1978 Nobel Prize for Chemistry. The
cause(s) for this closure are subject to interpretation. Most
biochemistry textbooks as well as Weber (2002, 2005) cite a famous
experiment by Ephraim Racker and Walter Stoeckenius (1974) as crucial
for establishing Mitchell's mechanism. These biochemists worked with
synthetic membrane vesicles into which they had inserted purified
enzymes, one of which being the mitochondrial ATPase (the enzyme
directly responsible for phosphorylation of ADP). The other enzyme was
not derived from mitochondria at all, but from a photosynthetic
bacterium. This enzyme had been shown to function as a light-driven
proton pump. When this enzyme was inserted into artificial membrane
vesicles together with the mitochondrial ATPase, the vesicles
phosphorylated ADP upon illumination.



This experiment was viewed as crucial evidence for the chemi-osmotic
mechanism because it was the first demonstration that the ATPase can
be powered by a chemiosmotic gradient alone. The involvement of a
chemical intermediate could be ruled out because there were no
respiratory enzymes present to deliver an unknown intermediate to the
ATPase.



The Racker-Stoeckenius experiment is perhaps best viewed as a
straightforward case of an *eliminative induction*. On this
view, the experiment decided between two causal graphs:



 (1)
 respiration - proton gradient - phosphorylation


The alternative causal graph was:



 (2)
 proton gradient - respiration - chemical high-energy
intermediate - phosphorylation


The experiment showed a direct causal link from the protein gradient
to phosphorylation, which was consistent with (1) but not with (2),
thus (2) was eliminated. However, it is clear that Duhem-style
skeptical doubts could be raised about this case. From a strictly
logical point of view, even if the experiment ruled out the chemical
hypothesis, it didn't prove Mitchell's hypothesis.



So why have biochemists emphasized this experiment so much? Perhaps
the reason is not merely the beauty of the experiment or its
pedagogical value. From a methodological point of view, the experiment
stands out from other experiments in the amount of control that
biochemists had of what was going on in their test tubes. Because it
was an artificially created system assembled from purified components,
the biochemists knew exactly what they had put in there, making it
less likely that they were deceived by traces from the enormously
complex system from which these biochemical agents were derived. On
such an interpretation, the experiment was not crucial in
Duhem's sense of ruling out all alternative hypotheses. Rather,
what distinguishes it is that, within the body of evidence that
supported Mitchell's hypothesis, this one reached an
unprecedented standard of experimental rigor, making it more difficult
for opponents of Mitchell's hypothesis to challenge it (see
Weber 2005, Chapter 4).


### 2.2 DNA Replication and Inference to the Best Explanation



As another example, consider the models for DNA replication that were
proposed in the 1950s after the publication of the double helix
structure of DNA by J.D. Watson and F.R.H. Crick (Lehninger 1975):



![image from Lehninger 1975](lehninger.jpg)
Figure 1.




In purely causal terms, what all these models show is that the
sequence of nucleotides in a newly synthesized DNA molecule depends on
the sequence of a pre-existing molecule. But the models also contain
*structural* information such as information the DNA double
helix topology and the movements undergone by a replicating DNA
molecule (still hypothetical at that time). According to the model on
the left, the so-called "conservative" model, the two
strands of the DNA double helix do not separate prior to replication;
they stick together and the daughter molecule grows along an intact
double helix that acts as a template as a whole. According to the
model in the middle, called the "semi-conservative"
mechanism (believed to be correct today), the two strands do separate
in the process. The newly synthesized strands grow along the separated
pre-existing strands that each acts as templates. On the model on the
right, the "dispersive" model, the two strands not only
separate in the process, they are also cut into pieces that are then
rejoined. While pure causal graphs (i.e., causal graphs that contain
only information about what variables depend on what other variables
causally) may be used to depict the causes of the separation and
cutting events in semi-conservative and dispersive model, it also
takes a description of the structure of the DNA molecule, including
the topology and relative movements of the strands at different stages
of the replication process. This is genuine mechanistic information
that must supplement the information contained in the causal graphs in
order to provide a normatively adequate mechanistic explanation.



How can such a mechanism be tested? To see this, it is illuminating to
consider the famous experiment that is said to have enabled a choice
between the three DNA replication mechanisms in 1957. Also known as
"the most beautiful experiment in biology" (Holmes 2011),
this experiment was carried out by Matthew Meselson and Frank Stahl by
using an analytic ultracentrifuge (see also the discussion of
the Meselson-Stahl experiment in the entry
 experiment in physics).



Meselson and Stahl grew bacteria in a growth medium that contained a
heavy nitrogen isotope, 15N. These bacteria were then
transferred to a medium with normal light nitrogen, 14N.
After one generation, the bacteria were harvested and their DNA was
extracted and loaded onto a caesium chloride solution in the
ultracentrifuge chamber (Fig. 2). Caesium atoms are so heavy that they
will form a concentration gradient when subjected to high centrifugal
forces. In such a gradient, DNA floats at a band in the gradient where
the molecular density corresponds to that of the caesium chloride
solution. Thus, the analytic centrifuge is an extremely sensitive
measuring device for molecular density. In fact, it is sensitive
enough to detect the difference between DNA that contains heavy
nitrogen and DNA that contains light nitrogen. It can also distinguish
these two DNA species from a hybrid made of one strand containing
heavy nitrogen and one strand containing light nitrogen. Indeed, after
one round of replication, the bacterial DNA in Meselson's and Stahl's
experiment was of intermediate density. After another round, the DNA
had the same density as DNA in its natural state.



![depiction of the Meselson-Stahl experiment](watson.jpg)
Figure 2.
The Meselson-Stahl experiment. The depiction of the centrifuge is
misleading; Meselson and Stahl were using a sophisticated analytic
ultracentrifuge, not a swinging bucket preparatory centrifuge as this
picture suggests. Furthermore, this representation of the experiment
already contains its theoretical interpretation (Watson
1965).[1]




The outcome was exactly what one would expect on the basis of the
semi-conservative model: After one round of replication, the DNA is
exactly of intermediate density because it is a hybrid of a heavy and
a light strand (containing heavy or light nitrogen, respectively).
After another round, a light molecule appears which contains no heavy
nitrogen. With the exception of the heavy/light hybrid, there are no
other molecules of intermediate density (as one would expect on the
dispersive scheme).



Even though this really looked like a spectacular confirmation of the
semi-conservative scheme, Meselson and Stahl (1958) were quite
cautious in stating their conclusions. Avoiding theoretical
interpretation, all the experiment showed was that base nitrogen
distributes evenly during replication. While this is inconsistent with
the dispersive mechanism, it did not rule out the conservative
mechanism. For it was possible that the material of intermediate
density that the ultracentrifuge's optical devices picked up did not
consist of hybrid heavy/light DNA molecules at all, but of some kind
of complex of heavy and light DNA. For example, Meselson and Stahl
speculated that end-to-end covalent associations of old and newly
synthesized DNA that was produced by the conservative mechanism would
also have intermediate density and therefore produce the same band in
their experiment. For this reason, could not completely rule out an
interpretation of the results in terms of the conservative
mechanism.



Meselson's and Stahl's caution was well justified, as we know now. For
they did not know exactly what molecular species made up the bands
they saw in their CsCl gradients. More recent considerations suggest
that their DNA must have been fragmented, due to Meselson's and
Stahl's use of a hypodermic needle to upload the DNA on their
gradients. Such a treatment tears a whole genome from *E. coli*
into little pieces. This fragmentation of the DNA would have ruled out
the alternative interpretation with end-to-end linked molecules, had
the scientists been aware of it at the time. In fact, without the
shearing of the DNA before the density measurement the whole
experiment wouldn't have worked in the first place, due to the
circular structure of the *E. coli* chromosome, which affects
its density (Hanawalt 2004). What this shows is that there were
relevant facts about the experimental system that Meselson and Stahl
did not know, which makes it difficult to view this experiment as
crucial.



Nonetheless, it is possible to view the experiment as performed in
1957 as strong evidence for the semi-conservative mechanism. Weber
(2009) argues that this mechanism is *part of the best
explanation* of Meselson's and Stahl's data. By
"data", Weber means the actual bands observed. Why is this
explanation better than the one involving the conservative scheme and
end-to-end associations of heavy and light DNA? To be
*consistent* with some data is not the same as being *a good
explanation* of the data. The explanation using the
semi-conservative scheme was better because it showed directly how the
nitrogen is distributed evenly. By contrast, the alternative
explanation requires the additional assumption that the parental and
filial DNA somehow remain covalently attached together after
replication. This assumption wasn't part of the mechanism, therefore
the latter explanation was incomplete. A complete explanation is
always better than an incomplete one; no principle of parsimony need
be invoked here.



The case can thus be reconstructed as an inference to the best
explanation (Lipton 2004), or perhaps preferably as an inference to
the only explanation (Bird 2007). Inference to the best explanation
(IBE), also known as abduction, is a controversial inductive inference
scheme that selects from a set of candidate hypothesis the one that
best explains the phenomena.



A variant of IBE is also used by Cresto (2008) to reconstruct the
experiment by Avery that showed that the transforming principle in
pneumococcus is DNA rather than protein. However, her conclusion is
that, in this case, IBE is inconclusive. What it does show is that
there was a rational disagreement, at the time, on the question of
whether DNA was the transforming principle. Novick and Scholl
(forthcoming) argue that Avery et al. were not relying on IBE; they
actually had a stronger case conforming to the traditional vera causa
ideal (see Section 5.2).



To sum up, we have seen that a methodological analysis of some of
biology's most famous experiments reveals many intricacies and
lacunae in their evidential force, which makes it difficult to see
them as "crucial experiments". However, a rationale other
than their pedagogical value can often be given for why the textbooks
accord them a special epistemic status.


## 3. Experimental Systems and Model Organisms



The last two sections have treated experiments primarily as ways of
testing theoretical hypotheses and causal claims, which is where
traditional philosophy of science saw their principal role. However,
there exists a considerable body of scholarship in the history and
philosophy of biology that shows that this does not exhaust the role
of experiments in biology. Experimentation, to echo Ian Hacking's
famous slogan, "has a life of its own" (Hacking 1983).
Much that goes on in a biological laboratory does not have the goal of
testing a preconceived theory. For example, many experiments play an
*exploratory* role, that is, they assist scientists in
discovering new phenomena about which they may not yet have any
theoretical account or not even any clear ideas. Exploratory
experimentation has been investigated in the history and philosophy of
physics (Steinle 1997) as well as biology (Burian 1997, 2007; O'Malley
2007; Waters 2007). These studies show that the development of any
discipline in experimental biology cannot be understood by focusing on
theories and attempts to confirm or refute these theories.
Experimental practice is simply not organized around theories,
particularly not in biology. If this is so, we must ask in what other
terms this practice can be explained or reconstructed. Recent
scholarship has focused in particular on two kinds of entities:
*model organisms* and *experimental systems*.


### 3.1 Model Organisms



What would modern biology be without its model organisms? To give just
a few examples: Classical genetics was developed mainly by
experimenting with fruit flies of the species *Drosophila
melanogaster*. The same organism has recently also been at the
center of much exciting work in developmental biology, together with
the nematode *Caenorhabditis elegans* and the zebrafish
*Danio rerio*. Molecular biologists were initially mostly
working with the bacterium *Escherichia coli* and bacteriophage
(viruses that infect bacteria). Neuroscientists owe much to the squid
with its giant axons. For immunology, the mouse *Mus musculus*
has proven invaluable. Plant molecular biology's favorite is
*Arabidopsis thaliana*. Cell biology has found in baker's yeast
*Saccharomyes cerevisiae* an organism that is as easy to breed
as *E. coli*, but its cells are more similar to animal and
human cells. This list could go on, but not forever. Compared to field
biology, the number of species that are being studied in the
experimental life sciences is quite small; so small, in fact, that for
most of these model organisms complete genomic DNA sequences are
available today.



It may seem as somewhat paradoxical that it is exactly these
experimental disciplines of biology that limit their research to the
smallest part of life's diversity that aspire to the greatest degree
of universality. For the point of studying model organism is often to
gain knowledge that is not only valid for one species but for many
species, sometimes including humans. Before discussing this
epistemological question, it is pertinent to review some results of
historical and philosophical analyses of research on model
organisms.



An important study is Robert Kohler's *Lords of the Fly*
(Kohler 1994), a history of *Drosophila* genetics originating
from Thomas Hunt Morgan's laboratory at Columbia University. Kohler
attributes the success of this way of doing science to the enormous
output of the *Drosophila* system in terms of newly described
and mapped mutations. The fruit fly breeds relatively fast and is easy
to keep in laboratories in large numbers, which increases the chance
of detecting new mutations. Kohler refers to Drosophila as the
"breeder-reactor" to capture this kind of fecundity, thus,
his study is not unlike an ecology of the lab fruit fly. The elaborate
techniques of genetic mapping developed in Morgan's laboratory, which
assigned each mutation a physical location on one of the fly's four
chromosomes, can also be viewed as a way of organizing laboratory work
and keeping track of the zillions of mutants that were cropping up
continuously. A genetic map is a systematic catalogue of mutants and
thus a research tool as much as it is a theoretical model of the fly's
genetic system (cf. Weber 1998). Thus, most of what went on in
Morgan's laboratory is best described as breeding, maintaining,
characterizing and cataloguing (by genetic mapping) fly strains. Very
little of it had anything to do with testing genetic theories, even
though the theoretical knowledge about regularities of gene
transmission canonically known as "Mendel's laws" was, of
course, also considerably refined in the process (Darden 1991).
However, classical genetic theory was also a means of discovering
mutants and genes for further study, not an end in itself (Waters
2004). This is also evident in the way in which *Drosophila*
was adapted to the age of the molecular biology (Weber 2005; Falk
2009).



Model organisms were often chosen for a particular field of study, but
turned out to be invaluable for other fields as well.
*Drosophila* is a case in point; Morgan was mainly interested
in embryology when he chose *Drosophila* as a model system.
This paid off enormously, but the fly was just as important for
genetics itself, including evolutionary genetics (especially the work
of one of the "architects" of the evolutionary synthesis,
T. Dobzhansky; see Dobzhansky 1937), behavioral genetics (e.g., S.
Benzer's studies of the circadian clock mechanism, see Weiner 1999),
biochemical genetics, as well as neuroscience.



There is always an element of contingency in the choice of model
organisms; no biological problem determines the choice of the best
organism to study it. Even though considerations of convenience, easy
breeding and maintenance, as well as suitability for the study of
specific phenomena play a role (Clarke and Fujimura 1992; Burian 1992,
1993; Lederman and Burian 1993; Clause 1993; Creager 2002; Geison and
Creager 1999; Lederman and Tolin 1993), there are always many
different organisms that would satisfy these criteria. Thus, which
model organism is chosen sometimes is a matter of chance.



Is it possible that our biological knowledge would be altogether
different, had contingent choices been different in the past? As this
question requires us to indulge in historical counterfactuals, which
are controversial (Radick 2005), it is difficult to answer. However,
it may not matter much one way or the other if the knowledge produced
by model organisms can be shown to be of general validity, or at least
as transcending the particular organism in which it was produced. This
is an instance of the more general epistemological problem of
extrapolating knowledge from one domain into another and can be
fruitfully discussed as such (Burian 1992).



Let us first consider a special case, the universality of the genetic
code. In molecular biology, unlike in popular science articles, the
term "genetic code" does not refer to an organism's
genomic DNA sequence but to the assignment of amino acids to base
triplets on the messenger RNA. There are four such bases: A, U, G and
C. Three bases together form a "codon" and specify an
amino acid, for example, the triplet AUG specifies the amino acid
methionine (it is also a start codon, i.e., it initiates an open
reading frame for making a protein). It was remarkable to find that
the genetic code is completely identical in almost every organism that
has been studied so far. There are only a few exceptions known, for
example, the genetic code of mitochondria and chloroplasts or that of
Trypanosomes (a human parasite causing sleeping sickness). Therefore,
the code is called "universal", because the exceptions are
so few. But how do biologists know that the code is universal, given
that it has been determined only in a small number of species?



In this case, a simple Bayesian argument can be used to show that
current belief in the universality of the genetic code is well
justified. To see this, it must first be noted that the code is
arbitrary; there is no necessity in the specific mapping of amino
acids to codons in the current standard genetic code. A second premise
is that there is an enormously large number of different possible
genetic codes. Now, we may ask what the probability is that the exact
same genetic code evolved independently in so many different species
as have been investigated at the molecular level to date. Surely, this
probability is vanishingly small. The probability of coincidence of
genetic codes is much, much larger on the assumption that the code did
not arise independently in the different species. On this hypothesis,
the code arose only once, and the coincidence is due to common
descent. However, once a specific genetic code is in place, it is very
difficult to change, because any mutational change in the amino
acid-codon assignment tends to affect a larger number of different
proteins and thus threatens to kill the organism. It is for this
reason that Jacques Monod (1974) has described the code as a
"frozen accident". Its mutation rate is just very, very
low. These considerations together support the hypothesis of
universality in the case of the genetic code.



Such an argument may not always be available. In fact, in the general
case extrapolation from a model organism is intrinsically problematic.
The main problem is what Daniel Steel (2008) has termed the
"extrapolator's circle". The problem is this. We want to
infer that some system S has a mechanism M because another system T is
already known to have M. For this inference to be good, we must assume
that S and T are relevantly similar. We can't know that the systems
are relevantly similar unless we already know that they both have M.
But if we knew that, there would not be a need for extrapolating in
the first place.



Note that such a circle does not arise when we extrapolate genetic
codes. In this case, we *do* know that the systems are
relevantly similar because all organisms share a common ancestor and
because the code is hard to change. What can we do if no such argument
is available?



Steel (2008) has proposed a form of reasoning that he calls
"comparative process tracing". Steel's proposed solution
is that even in the absence of strong evidence as to what mechanism(s)
operate in a target system compared to a model system, scientists can
compare the two systems with respect to certain crucial nodes in the
respective causal structures, namely those where the two systems are
most likely to differ. This can break the regress by providing
evidence that the two systems are similar enough to warrant
extrapolations, yet it is not necessary to already have an
understanding of the target systems that matches the knowledge about
the model system.



While this reasoning strategy seems plausible, it may not be so
pertinent for extrapolating from model organisms. Steel's reasoning
strategy pertains to cases where we want to infer from one system
where we know a certain mechanism operates to a different kind of
system about we do *not* (yet) know that the same mechanism
operates. However, in biology there is often evidence to the effect
that, in fact, very similar mechanisms operate in the model as well as
in the target system. A particularly important kind of evidence is the
existence of so-called sequence homologies between different
organisms. These are usually DNA sequences that show a more or less
strong similarity, in some cases even identity. As it is (like in the
case of the genetic code discussed above) not likely that this
sequence similarity is due to chance, it is normally attributed to
common ancestry (hence the term sequence "homology"; in
biology, this term in its modern usage indicates relations of shared
ancestry). Sequence homology has proven to be a reliable indicator of
similarity of mechanisms. To give an example, a highly conserved
sequence element called the "homeobox", which was first
described in *Drosophila*, is today believed to play a similar
role in development in an extremely broad range of organisms (Gehring
1998). When there are reasons to think that the model and the target
share similar causal mechanisms due to common descent, the
extrapolator's circle does not arise.



However, the extent in which extrapolations from model organisms to
other organisms can serve as evidence in the context of justification
or merely as a heuristic in the context of discovery remains
controversial. Baetu (1916) argues for a middle ground according to
which extrapolations can be lines of evidence, but only in the context
of a larger body of evidence where certain assumptions made in
extrapolations are subjected to empirical scrutiny.



There has also been some debate to what extent there is a strong
parallel between model organisms and theoretical models in science,
for example, the Lotka-Volterra predator-prey model in population
ecology. A strong parallel is suggested by the fact that there is a
widespread agreement in the literature on scientific modeling (see
entry Models in Science) that scientific models need not be abstract
(i.e., consist of mathematical equations or something of this sort);
they can also be concrete and physical. Watson's and
Crick's 1953 DNA model made of cardboard and wire qualifies as a
model in this sense. Could a fruit fly bred in a laboratory to do
genetic experiments also be considered as a scientific model in the
standard sense? Ankeny and Leonelli (2011) answer this question in the
affirmative, on the grounds that (1) model organisms are used to
represent a whole range of other organisms and (2) that they are used
to represent specific phenomena.



Levy and Currie (2015) have criticized this idea. On their view,
scientific models such as Lotka's and Volterra's (and all
the other models discussed in the burgeoning modeling literature) play
a completely different role in science than model organisms. In
particular, they differ in the way they are used in scientific
inferences. In a model such as the mathematical predator-prey model,
scientists draw analogical inferences from model to target, inferences
that are underwritten by theoretical assumptions. By contrast, model
organisms serve as a basis for extrapolations from individual members
to a whole class (often but not necessarily on the basis of shared
ancestry). Thus, they want to exclude what they call "empirical
extrapolation" (a form of induction), which they take to be
characteristic for model organism-target inferences from the kind of
theoretical inferences that are used to gain knowledge about a target
via scientific models in general.



However, this does not mean that living organisms or populations of
organisms cannot be used as models. Levy and Currie accept that
certain model systems in experimental ecology and experimental
evolution are scientific models that are akin to the Lotka-Volterra
model. A case in point are Thomas Park's (1948) famous
competition experiments using the flour beetle Tribolium. What
characterizes such experimental models, in contrast to model
organisms, is that they can be used to represent generalized
biologically phenomena (e.g., interspecific competition in
Park's case) that can be applied to radically different and
taxonomically unrelated target systems (see also Weber 2014).



No matter whether model organisms are considered as scientific models
or as something else, it is widely agreed that they serve many
different purposes, only some of which are representational. The
development of model organisms such as *Drosophila* (fruit
fly), *Arabidopsis* (Thale cress), *Caenorhabditis*
(roundworm) and the associated databases such as FlyBase, Wormbase
etc. has had a profound impact on the way in which biological research
is organized (e.g., Geison and Creager 1999, Clarke and Fujimura 1992,
Creager 2002, Leonelli and Ankeny 2012). Furthermore, model organisms
are also important sources of research materials such as genetically
well-defined laboratory strains or genetically modified organisms
without which cutting-edge biological experimentation is no longer
possible today. Weber (2005) has introduced the notion of preparative
experimentation to capture this role of model organisms.


### 3.2 Experimental Systems



As we have seen, model organisms have greatly shaped the development
of experimental biology, and continue to do so. Another important
entity are so-called experimental systems. These are not to be
confused with model organisms: The latter is a biological species that
is being bred in the laboratory for experimental work. An experimental
system may involve one or several model organisms, and most model
organisms are used in several experimental system. An experimental
system typically consists of certain research materials (which may be
obtained from a model organism), preparatory procedures, measurement
instruments, and data analysis procedures that are mutually adapted to
each other.



Experimental systems are the core of Hans-Jorg Rheinberger's
(1997) account of mid-20th Century research on protein
synthesis. Rheinberger characterizes experimental systems as
"systems of manipulation designed to give unknown answers to
questions that the experimenters themselves are not yet clearly to
ask" and also as "the smallest integral working units of
research" (Rheinberger 1997, 28). He argues that research in
experimental biology always "begins with the choice of a system
rather than with the choice of a theoretical framework" (p. 25).
He then follows a certain experimental system through time and shows
how it exerted a strong effect on the development of biology. The
system in question is a so-called in-vitro system for protein
synthesis that was developed in the laboratory of Paul Zamecnik at
Massachusetts General Hospital in the 1950s. "In vitro"
means that the system doesn't contain any living cells. It is rather
based on a cell extract, originally from bacteria, later also from
other organisms including rabbits and yeast. The cell extract is
prepared in a way that preserves functionality of the protein
synthesis machinery. Instead of the RNAs that naturally occur in the
source organism, the in-vitro system may be "programmed"
with exogenous or even artificial RNA. Furthermore, the experimental
system contains measurement procedures (sometimes called
"assays" in experimental biology) for protein synthesis
activity. One such method is to measure incorporation of radioactivity
introduced by amino acids containing a radioisotope such as sulfur-35,
but there were other methods as well. Probably the most famous
experiment done with such a system is the experiment by Marshall
Nirenberg and Heinrich Matthaei (1961). These researchers added an
artificial RNA, namely poly-U (U or uracil is one of the four bases of
RNA) to the in-vitro system and showed that it produced a polypeptide
(=protein) containing only the amino acid phenylalanine. Thus, they
"cracked" the first "word" of the genetic
code, namely UUU for phenylalanine.



One of the central points of Rheinberger's analysis is that the
in-vitro system was never designed to do this task. Its original
purpose was to study protein synthesis in cancer cells. In addition to
unraveling the genetic code and the mechanisms of protein synthesis,
it was later used for various other purposes in biochemistry and cell
biology (for example, for studying the transport of proteins across
endoplasmic reticulum and mitochondrial membranes). The system was
thus not even confined to a single discipline, in fact, it to some
extent lead to a re-organization of scientific disciplines.
Furthermore, the system was also fused with other experimental system
or it bifurcated into different systems. Experimental systems, like
model organisms are at least as important as focal points that
organize research as theories.



While Rheinberger's account of experimental research in biology is
right to put its emphasis on experimental systems rather than on
theories, it may be criticized for the ontology of experimental
systems that it contains. On this account, experimental systems are
construed as very inclusive entities. They contain not only the
specific materials and apparatus necessary to do research, but also
the preparatory procedures, lab protocols, storage devices,
measurement techniques, and so on. Thus, it is clear that such systems
are not only composed of material entities; at least some of the
constituents of experimental systems are *conceptual* in
nature. For example, a lab protocol that describes how to prepare a
cell extract that will be able to carry out protein synthesis in vitro
is really a conceptual entity. A researcher who is following such a
protocol is not merely manipulating materials, lab equipment or
symbols. Rather, she is acting under the guidance of concepts. (Action
is always behavior guided by concepts). Among these concepts there may
be what used to be known as "observation concepts" such as
"supernatant", "pellet", "band",
and so on. Furthermore, the protocol will contain terms such
"microsomal fraction", which is supposed to designate a
certain sediment produced by centrifugation that contains microsomes
(vesicles of endoplasmic reticulum membrane). Thus, the protocol also
contains *theoretical terms*.



Rheinberger refers to theoretical entities as "epistemic
things". This concept signifies the "material entities or
processes--physical structures, chemical reactions, biological
functions--that constitute the objects of inquiry"
(Rheinberger 1997, 28). Epistemic things can unexpectedly appear and
disappear, or be re-constituted in new guises as experimental systems
are developed. Sufficiently stabilized epistemic things can
"turn into the technical repertoire of the experimental
arrangement" (1997, 29) and thus become "technical
objects." One of Rheinberger's examples of an epistemic thing is
the ribosome (a comparatively large molecular complex of protein and
RNA that catalyzes some of the crucial steps in protein synthesis).
Here, it can be argued that whether or not some experimental setup
contained ribosomes is a *theoretical judgment*. Thus, an
experimental system contains materials and apparatus as well as
observation concepts and theoretical concepts. They are rather
heterogeneous ontologically.



If jumbles are considered undesirable from an ontological point of
view, it is also possible to construe experimental systems as
*purely* conceptual entities. They are ways of acting in a
laboratory, and action is always guided by concepts. Material things,
insofar as they appear in experimental practice, are only parts of an
experimental system to the extent in which they are subject to
purposeful experimental action. They can only be subject to such
action to the extent to which they are recognized by an experimenter,
for example, as a microsomal fraction or an antiserum with a certain
antigen specificity, and so on. A biological sample without its label
and some researcher who knows what this label means is of no value
whatsoever; in fact, it isn't even a biological sample.



It can thus be argued that it's really thought and concepts that give
an experimental system its identity and persistence conditions;
without concepts it's really just a loose assemblage of plastic,
glass, metal, and dead stuff coming out of a blender. On such a view,
experimental systems are not "out there" as
mind-independent parts of a material reality; they exist only within
some concept-guided practice.


## 4. Experimentation, Rationality and Social Epistemology



As the preceding sections should have made clear, there is ample
evidence that biological research does not fit a Popperian image of
science according to which "The theoretician puts certain
definite questions to the experimenter, and the latter, by his
experiments, tries to elicit a decisive answer to these questions, and
to no others. All other questions he tries hard to exclude"
(Popper 1959, 107). According to Rheinberger, much experimental
research in biology does not aim at testing pre-conceived theories.
However, sometimes theories or theoretical frameworks are, in fact,
adopted by the scientific community, while others are abandoned. Even
if it is true that most research is not aimed at testing theories,
research can still undermine some theoretical ideas and support
others, to the point that one framework is chosen while another is
rejected. How are such choices made? What principles guide them? And
do the choices actually exhibit some kind of epistemic rationality, as
most philosophers of science think, or do they merely reflect the
interests or larger cultural changes in society, as many sociologists
and historians of science think?



Questions such as these are notoriously difficult to answer. Those who
prefer a rational view of scientific change must demonstrate that
their preferred epistemic norms actually inform the choices made by
scientists. This has proven to be difficult. If we re-consider our
case from Section 3, the oxidative phosphorylation controversy, there
exists a sociological account (Gilbert and Mulkay 1984) as well as
different philosophical accounts that do not even agree in how to
explain scientific change (Allchin 1992, 1994, 1996; Weber 2005, Ch.
4-5).



By the same token, those who think that scientific change is
historically contingent, in theory, must be able to justify historical
counterfactuals of the form "had the social/cultural context at
some given time been different, scientists would have adopted other
theories (or other experimental systems, model organisms, etc)".
It is controversial whether such claims are justifiable (see Radick
2005 for a recent attempt).



Perhaps there is a way of reconciling the two perspectives. In recent
years, a new kind of epistemology has emerged that sees no
contradiction in viewing science both as a profoundly social activity
and at the same time as rational. This, of course, is social
epistemology (e.g., Goldman 1999; Longino 2002; Solomon 2001). Social
epistemologists try to show that social interactions in scientific
groups or communities can give rise to a practice that is rational,
although perhaps not in exactly the same way as epistemological
individualists have imagined it.



Could there be a social account of scientific change for experimental
biology? Of course, such an account should not fall back into a
theory-first view of science but rather view theories as embedded in
some practice. To see how this is possible, it's best to consider the
case of classical genetics.



Classical genetics is said to derive from Mendel's experiments with
pea plants, however, the story is more complex than this. At the
beginning of the 20th Century, there existed several
schools in genetics, on both sides of the Atlantic. In England, the
Biometric school of Karl Pearson and Raphael Weldon were developing a
quantitative approach that took Francis Galton "Law of ancestral
heredity" as its point of departure. The Mendelian William
Bateson was leading a rival movement. In the United States, Thomas
Hunt Morgan and his associates were constructing the first genetic
maps of the fruit fly. For a while, William Castle was defending a
different approach to genetic mapping, as well as a different theory
of the gene. Various approaches were also developed in Continental
Europe, for example, in the Netherlands (Hugo de Vries), Germany (Carl
Correns) or Austria (Erich Tschermak). The American school of Thomas
Hunt Morgan pretty much carried the day. Its approach to mapping genes
as well the (ever changing) theory of the gene became widely accepted
in the 1930s, and became officially incorporated in the Evolutionary
Synthesis of the 1930s and 40s (Mayr 1982; Provine 1971).



A traditional way for a philosopher of science of looking at this case
would be to consider the salient *theories* and to ask: What
evidence compelled scientists to adopt Morgan's theory? However, this
may not be the right question to ask. For this question makes the
silent supposition that theories and experimental evidence can be
separated from each other in genetics. But it can be argued that the
two depend too strongly on each other to be considered separate
entities. Classical genetics--in all its forms--was first
and foremost a way of doing crossing experiments with various model
organisms, and to arrange the results of these experiments in a
certain way, for example, linear genetic maps. To be sure, there were
also certain ideas about the nature of the gene, some of which highly
speculative, others well established by experiments (for example, the
linear arrangement on the chromosome, see Weber 1998b). But what is
sometimes referred to as "the laws of transmission
genetics" or simply "Mendel s laws" was part
and parcel of a certain way of doing genetics. Thus, theory is not
separable from experimental practice (Waters 2008). This, of course,
cuts both ways: Experimental data in genetics are as
"theory-laden" as they are in other sciences, in other
words, the analysis and interpretation of experimental data require
theories.



For our current issue of scientific change, what this means is that
theory and experimental evidence were selected *together*, not
the former on the basis of the latter (as a naive empiricist account
would have it).



On what grounds was this selection made? And who made it? A simple,
but perhaps incomplete explanation is that the Morgan approach to
genetics was selected because it was the most fruitful. A skilled
geneticist who adopted the Morgan way was almost guaranteed to come up
with publishable results, mostly in the form of genetic maps, and
perhaps also some interesting observations such as mutations that
behaved oddly in genetic crosses. By contrast, the alternative
approaches that were still around in the early 20th Century
did not prove to be as fruitful. That is, they did not produce a
comparable number of results that could be deemed a success according
to these sciences' *own* standards. What is more, the
alternative genetic approaches were not adaptable to other scientific
disciplines such as evolutionary biology. Classical genetics thus
out-competed the other approaches by its sheer productivity, which was
manifested by published research papers, successful grant
applications, successful students, and so on. It was therefore the
scientific community as a whole that selected the new genetics due to
its fruitfulness. At no point was there any weighing of evidence for
or against the theoretical framework in question on the part of
individual scientists, or at least this played no role (of course,
there was weighing of evidence for more specific claims made within
the same framework). Theories in experimental biology are thus
selected as parts of experimental practices (or experimental systems,
see
 SS4.2),
 and always at the community level. This is how a social
epistemological account of scientific change in experimental biology
might look like (Weber 2011).



The image of the rise of classical genetics just drawn is reminiscent
of Thomas Kuhn's philosophy of science (Kuhn 1970), or of David Hull's
account of the rise of cladistic taxonomy (Hull 1988). It is a
controversial issue whether such an image is compatible with a broadly
rational construal of scientific practice. Kuhn thought that there
exists no external standard of rationality that we could appeal to in
order to answer this question, but he also held that science is the
very epitome of rationality (Kuhn 1971, 143f.). According to Kuhn,
there is an emergent social rationality inherent in modern science
that cannot be construed as the exercise of individual rational
faculties. Hull (1988) seems to be taking a similar view.


## 5. Experimental Artifacts and Data Reliability


### 5.1 Robustness



Under what conditions should scientists trust experimental data that
support some theoretical conclusion such as, for example, that DNA has
a helical structure or that mitochondria are bounded by two layers of
membrane? This is known as the problem of "data
reliability". Unreliable data are commonly referred to as
"experimental artifacts" in biology, indicating their
status as being "made" by the experimental procedure. This
is somewhat misleading, as all data--whether they are reliable or
artifacts--are made by the experimental procedure. The difference
is that reliable data are correct representations of an underlying
reality, whereas so-called artifacts are incorrect representations.
This characterization assumes that data have some sort of
representational content; they represent an object *as*
instantiating some property or properties; (see Van Fraassen 2008, Ch.
6-7). The question of what it means for data to represent their
object correctly has not been much discussed in this context. The
focus so far has been mostly on various strategies for checking data
for reliability, which will be discussed below. As for scientists
themselves, they tend to place this problem under the rubric of
replicability. While this is also an important topic, the fact that
some data are replicable is not sufficient for their reliability.
There are lots of well-known examples of perfectly replicable data
that turned out to be not reliable, e.g., the case of the mesosome to
be discussed below.



One of the more influential ideas in philosophy of science is that of
robustness. Originally, the term was introduced to denote a certain
property of theoretical models, namely insensitivity to modeling
assumptions. A robust result in theoretical modeling is a result that
is invariant with respect to variations in modeling assumptions
(Levins 1966; Wimsatt 1981; Weisberg 2006). In experimental science,
the term means something else, namely that a result is invariant with
respect to the use of different experimental methods. Robust
experimental results are results that somehow agree even although they
have been produced by independent methods. The independence of methods
can mean at least two things: First, the methods use different
physical processes. For example, a light microscope and a
(transmission) electron microscope are independent methods in this
sense; the former uses visible light, the latter an electron beam to
gather information about biological structures. The second sense of
independence concerns the theoretical assumptions used to analyze and
interpret the data (most data are theory-dependent). If these
assumptions are different for the two methods, they are also referred
to as independent, or as independently theory-dependent (Culp 1995).
These two senses of "independent" usually coincide,
although there could be exceptions.



A much-discussed example of a robust experimental result from the
physical sciences is the numerical value obtained for Avogadro's
number (6.022 x 1023) at the beginning of the 20th Century
by using no less than thirteen independent methods according to the
physicist Jean Perrin (Nye 1972). Salmon (1984) has argued that this
provided a strong justification for belief in the existence of atoms
by way of a common-cause argument. On Salmon's view, the existence of
atoms can be inferred as the common cause of Perrin's thirteen
different determinations of Avogadro's number. Others have construed
robustness arguments more along the lines of Putnam's "no
miracle" argument for scientific realism, according to which the
assumption of the reality of some theoretical entities is the best
explanation for the predictive success of theories or, in the case of
robustness, for the agreement of experimental results (Weber 2005, Ch.
8; Stegenga 2009).



Various authors have tried to show that robustness-based reasoning
plays an important role in judgments about data reliability in
experimental biology. For example, Weber (1998b) argues that the
coincidence of genetic maps of *Drosophila* produced by
different mapping techniques provided an important argument for the
fidelity of these maps in the 1930s. Culp (1995) argued that
robustness provides a way out of a methodological conundrum know as
"data-technique circles", which is a more apt designation
for Collins' "experimenter's regress". According to
Collins (1985), scientists must trust data on the grounds of their
being produced by a reliable instrument, but they can only judge an
instrument to be reliable on the basis of it's producing the right
kind of data. According to Culp (1995), robustness provides a way out
of this circle. If the data obtained by independent methods agree,
then this supports both the reliability of these data and of the
instrument that produced these data. She attempts to demonstrate this
on the example of different methods of DNA sequencing.



Stegenga (2009) criticizes the approach from robustness. On his view,
what he calls "multi-modal evidence", i.e., evidence
obtained by different techniques, is often discordant. If it is
concordant, it is difficult to judge if the different methods are
really independent. However, Stegenga (2009) does not discuss Culp's
(1995) example of DNA sequencing, which seems to be a case where
evidence obtained by different sequencing techniques is often
concordant. Furthermore, Culp shows that the techniques are
independent in the sense that they are based both on different
biochemical processes and different theoretical assumptions.



A historical case that has been extensively discussed is the case of
the hapless mesosome. For more than 20 years (ca. 1960-1983),
this was thought to be a membrane-bound structure inside bacterial
cells, not unlike the nucleus or the mitochondria of the cells of
higher organisms. However, it could only be seen in electron
microscopy (bacterial cells being too small for light microscopy).
Because electron microscopy requires a vacuum, biological samples
require a lot of preparation. Cells must be chemically fixed, which
was done mostly by using Osmium tetroxide at the time. Furthermore,
the samples must be protected from the effects of freezing water. For
this purpose, cryoprotectants such as glycol must be used. Finally,
the material must be cut into extremely thin slices, as an electron
beam does not have much penetrating power. Electron microscopists used
two different techniques: The first involved embedding the cells in a
raisin before cutting with very sharp knives (so-called microtomes).
The other technique used fast freezing followed by fracturing the
cells along their membranes. At first, mesosomes were seen in electron
micrographs under a variety of conditions, but then there were
increasing findings were they failed to show. Thus, suspicion started
to rise that mesosomes were really a microscopic artifact. Ultimately,
this is what microbiologists and electron microscopists ended up
concluding by the mid-1980s, after more than two decades of research
on these structures.



There are different interpretations of this episode to be found in the
literature. One of the oldest is Rasmussen (1993), who basically
offered a sociological explanation for the rise and fall of the
mesosome. This account has been widely criticized (see Rasmussen 2001
for a more recent defense). Others have tried to show that this case
exhibits some methodological standard in action. On Culp's (1994)
account, the case demonstrates the relevance of the standard of
robustness in actual scientific practice. According to Culp, the
mesosome was accepted as a real entity so long as a robust (i.e.,
diverse and independently theory-dependent) body of data provided
signs of their existence. When the winds changed and the evidence
against the mesosome became more robust than the evidence in its
favor, it was dropped by biologists.



As this presentation should make clear, Culp's account requires that
robustness comes in degrees and that there should, therefore, be some
way of comparing degrees of robustness. However, no proponents of
robustness to date have been able to come up with such a measure.
Ultimately, what the case of the mesosome shows is that, in realistic
cases, the evidence for some theoretical entity is *discordant*
(Stegenga 2009), meaning that some findings supported the existence of
mesosomes whereas others did not. But this means that robustness as a
criterion cannot give unequivocal results, unless there is some way of
saying which body of data is more robust: the body that supported the
theoretical entity or the body which did not. Thus, when the evidence
is discordant the criterion of robustness fails to provide a solution
to the problem of data reliability.



An alternative account of the mesosome story has been offered by
Hudson (1999). Hudson argues that considerations of robustness did not
play a role in the scientists' decisions concerning the reality
of the mesosome. Had they, in fact, used such reasoning, they would
never have believed in mesosomes. Instead, they used a kind of
reasoning that Hudson refers to as "reliable process
reasoning". By this, he means basically that scientists trust
experimental data to the extent in which they have reasons to believe
that the processes that generated these data provide faithful
representations of reality. In the case of the mesosome, the evidence
from electron microscopes was first judged reliable. But later, it was
shown empirically that mesosomes were actually produced by the
preparation procedure. Briefly, it was shown by various experiments
that the chemical fixants used directly damage biological membranes.
The mesosomes were thus *shown* to be artifacts by empirical
methods. Considerations of robustness thus played no role in the
electron microscopists' data reliability judgments.



Similar to Hudson, Weber (2005, Ch. 9) argues that the demonstration
that mesosomes were experimental artifacts was nothing but an ordinary
experimental demonstration of the existence of a causal relationship,
namely between mesosome appearances and the fixation agents. Thus,
there may not be any special kind of reasoning other than ordinary
causal reasoning (see
 SS2.1)
 involved in data reliability judgments.



An aspect that has so far been largely neglected in this debate is a
different kind of robustness, namely *physical* robustness. If
we compare the case of the mesosomes with that of other intracellular
organelles, for example, the eukaryotic nucleus or mitochondria, it is
notable that it was never possible to isolate mesosomes, whereas the
latter organelles can be recovered in more or less intact form from
cell extracts, normally by the use of centrifugation. Although it is,
of course, entirely possible that the structures so recovered are
artifacts of the preparation procedure, there may be additional
evidence for their reality. For example, there could be telltale
enzyme activities that can be measured in isolated cell organelles
that correspond to the organelle's function. It might be possible to
subsume this kind of reasoning under Hacking's (1983) strategies of
using the ability to intervene with theoretical entities as a ground
for their real existence.


### 5.2 The Vera Causa Ideal



Recent scholarship has defended the traditional ideal of vera causa
both as a normatively adequate methodological standard for
experimental biology as well as a standard that biologists are
actually committed to. The ideal requires that scientific explanations
of a phenomenon cite true causes or verae causae. To qualify as a true
cause, an entity must satisfy the following criteria (e.g., Hodge
1992): First, it must have been shown to exist. Second, it must be
causally competent to produce the phenomenon in question. Third, it
must be causally responsible for this phenomenon. Importantly, the
evidence for existence must be independent from the evidence for
causal competence. Thus, the mere fact that an entity's
purported causal capacities are able to explain a phenomenon dies not
alone constitute sufficient evidence for its existence. What this
means, obviously, is that an inference to the best explanation (IBE)
of a phenomenon cannot alone justify acceptance of a postulated
entity. It must always be accompanied by independent evidence for
existence.



Proponents of the vera causa ideal thus oppose the idea that IBE might
be something like a common methodological standard for metaphysics and
for science. If metaphysicians rely on IBE to justify the entities
they postulate, for examples, tropes or substances (as argued by Paul
2012), they do not hold these beliefs to the same methodological
standard as scientists do (Novick forthcoming). For scientists are not
content with IBE-type arguments; they require something more before
they accept theoretical entities.



An example for the vera causa ideal at work can be found in the
history of genetics. In the 19th Century, there was much speculation
about hereditary particles. For example, Darwin's
"provisional hypothesis of pangenesis" postulated freely
circulating particles or "gemmules" that represented the
parts and organs of an organism and transmitted this information to
subsequent generations. While Darwin was himself an advocate of the
vera causa ideal, which he meticulously applied to his theory of
natural selection, he held this "provisional hypothesis"
to less exacting standards (Stanford 2006). However, of course others
criticized the pangenesis theory for its failure to meet the vera
causa standard, because the gemmules were only inferred on the grounds
that they could explain certain hereditary phenomena.



As Novick and Scholl (forthcoming) show, a science of genetics that
met the vera causa standard eventually emerged in the 20th century, in
the wake of the re-discovery of Mendel's laws as well as
improved microscopic and cytological techniques. The latter were
important, because they allowed independent checks of the structures
that were invoked in order to explain the observed experimental
regularities. A case in point is Thomas Hunt Morgan's and his
co-workers' "proof" of the hypothesis that genes are
parts of chromosomes (Bridges 2014). 



Morgan et al.'s argument made use of a phenomenon that is called
chromosomal non-disjunction. This term designates the failure of
sister chromosomes to segregate during the process of meiosis. A
possible result of this failure in Drosophila is a fly that has two
female sex chromosomes in addition to a male one (XXY). The
geneticists noticed that this would explain why some flies failed to
exhibit an inheritance pattern normally exhibited by traits that are
determined by sex-linked factors (i.e., factors that lie on one of the
sex chromosomes X or Y), namely "criss-cross" inheritance.
In this pattern, a recessive trait such as white eye color is
transmitted from the females of the first generation to the males in
the second generation, while the females revert to the original state
of red eyes, hence the expression "criss-cross". This
normal pattern is explained by the fact that a recessive X-linked
trait is always expressed in a male because there is only copy of the
corresponding gene in a male. The female offspring, by contrast,
receive a normal copy of the gene from their father, which is why the
recessive trait will be hidden.



In non-disjunction, some of the offspring carry an extra X in addition
to the male Y chromosome. This obliterates the criss-cross
mechanism.



Morgan and his group were adamant that neither the phenomenon of
sex-linked inheritance nor the fact that non-disjunction would explain
the observed deviations from this inheritance pattern were sufficient
to prove the chromosome theory. A necessary element in their case was
the cytology: The excessive X-chromosome was microscopically
observable, and it was shown to be present exactly in those flies that
failed to exhibit the criss-cross pattern. This is how the vera causa
ideal was met: The chromosomes as carriers of the genes not only
explained the phenomena, their existence was also supported by
evidence other than the fact that they explained the phenomena.
That's how they earned their place in biology's
ontology.



The vera causa ideal may also have been effective in the historical
episodes presented in previous sections. In the oxidative
phosphorylation case, the hypothetical chemical intermediate was never
accepted because biochemists failed to isolate and detect it.
Mitchell's chemi-osmotic gradient, by contrast, was readily
accepted. However, it's causal efficacy in powering
phosphorylation was doubted. This is where the Racker-Stoeckenius came
in: By demonstrating this causal efficacy, it completed the case for
chemiosmotic coupling in compliance with the vera causa ideal.



In a similar way, it can be argued that Meselson's and
Stahl's evidence for semi-conservative replication was
incomplete. The distribution of DNA in the density gradient supported
semi-conservative replication by IBE, but before the identity of the
the DNA molecules was confirmed the case was inconclusive, which is
why Meselson and Stahl were so cautious.