Judith,
Since you so kindly ask, here are two responses, at two (perhaps too many)
levels. My first reaction to Eva's posting is astonishment, puzzled at why
it is not proper to ask this question. Well, having read enough of
miscommunication (Watzlawick-- sp?) I won't spend time there. Instead what
you will get is an `ethnographic' self-interview.
Needless to say, I spent my commute this morning thinking about my responses,
especially in light of Jay's interest in Feyerabend, which I cannot address
in a separate message. My opinion of Feyerabend, though I enjoyed his
writing earlier in life, has constrained my participation in a discussion of
his work-- I have better things to do. I know I'm not Imre, yet the
discussion has turned into a slippery slope and will offer my opinions later
in this message.
Knowing what I do about Jay, being provocative that is, my supposition was
that he was being predictable. Yet, Jay's background crosses many barriers.
I know of his `talking science' work, and I know he participates in NARST
events and publication processes and of course his semiotic work and xmca
postings which favor Feyerabend and Latour. Through knowing these things, I
sometimes suspect that his epistemological postion could be almost anywhere.
(The ecological view that Eva mentions is like that of an external observer,
and seems to miss the epistemological details of knowledge development - how
the Scientist evaluates the status of knowledge.) My short answer is that my
work, though not so prestigious as Jay's, also crosses disciplines and have
found it fruitful to ask for clarification in discussion. If that is
sufficient you can skip the rest.
The long answer goes into my previous studies and requires brief explication
of my background. My doctorate and immediate subsequent work was in
_experimental_ atomic and molecular physics. As an undergraduate and
graduate student I was very interested in science methodology and pursued
through seminars and independent readings the works of Feyerabend, Kuhn,
Harre, Lakatos, Popper, and the EPR paradox literature which is too
voluminous to list here. Working for the 'Cognitive Development Project"
before becoming apprenticed to a physicist, my methodological turned
epistemological interests also led me to Frege, Russell, Wittgenstein, Kant,
von Glasersfeld and to Godel via Hofstadter, and cybernetic theories of
knowing.
As a physical scientist, I won't attempt to speak for other science
disciplines. My methodological studies influence my epistemological/cultural
views -- the endeavor of science as_a_way_of_knowing_. I agree with Eva,
science is a social practice. Yet like any other social practice, it is not
just any social practice. It has routines, ideologies, knowledge, and
artifacts that are particular to the motives. Mathematics is also a social
practice, which has routines, etc. some quite distinct from, and some in
common with, those of physical science (Steen, 1988, Lakatos `proofs and
refutations'). And so it goes.
_The external world has elevated ideological status in the social practice of
(physical) scientists._ The history of experiment is long and it's emergence
occurred at the historical separating point of science and philosophy (Power,
1664). Experiment -- testing ideas against the external world -- developed
as a method to resolve theoretical argument (Lakatos, 1978)). The work of
physical science is based upon an ontological and ideological premise "There
exists an external (physical) world" and then goes on to seek to describe the
phenomena of that physical world. The scientists that are not `traditional'
in Jay's view (luddites in my view) recognize the difference between theories
of the posited _external_ physical world and the way it really is, whatever
that is. What can be really confusing is that sometimes the premise, however
reasonable, is challenged.
The Einstein-Podolsky-Rosen paradox (Einstein et al., 1935) posed a conundrum
for physicists over the last half century. The authors posed several
seemingly reasonable requirements for physical theories such as `predicting
[a physical quantity] with certainty, without disturbing the system'. They
applied these with the mathematical apparatus of quantum mechanics in an
argument styled much like a reductio ad adsurdum and came to a contradiction.
Bell's work (Bell, 1988) took it a step further with predictions based upon
other underlying assumptions EPR made of the physical world that differed
from that of quantum mechanics (QM). Aspect's (reference not with me)
experimental data, followed by others', supported the predictions of quantum
mechanics.
Inherent in QM is the interpretation that we cannot test our knowledge of the
world, by the world, without disturbing the world. Since EPR was driven by
an ideology of objectivity, which still persists in same form only among
luddites, this greatly upset the authors. Their ideology: that elements of
physical theories must have corresponding elements in physical reality. It
is quite remarkable that so much work went on, theoretically at first, and
then finally driven to experiment, without regard to the results of Godel,
which describes the limitations of axiomatic systems like that used in the
EPR paper. The snark they were hunting turned into a boojum (Carol, --;
Mermin, 1990)
The ideology of objectivity must be reformulated in a statistical and
relational sense (except unfortunately in much public and science education
materials!) As I have alluded to in an earlier posting, verification of
experimental results, known as observer independence, theoretically and
experimentally, was and now remains a part of `objectivity'. The need for
verification is driven by the recognition of the very limitations of the
experimentalist and the experiment. The scientist strives towards
objectivity, but recognizes its faults. And a methodology remains, however
stronger.
Which leads me to Feyerabend. Unfortunately, Feyerabend's interest in
promoting the plurality of science methods (a position which I support) is
obscured by his `straw-man' (my attribution) polemic style, the latter
admitted to in his autobiography. Feyerabend conjures history and concludes
"anything goes" when that is not quite what he means. This results in a lot
of scientists who are outraged or offended in reaction that certainly seems
to impair the very progress Feyerabend wishes. Yet Feyerabend has also aimed
at a moving target, and has shot at where it used to be.
The AAAS science benchmarks better catch the essence of the _modern_
scientists view: `Scientific inquiry is more complex than popular conceptions
would have it. It is, for instance, a more subtle and demanding process than
the naive idea of "making a great many careful observations and then
organizing them." It is far more flexible than the rigid sequence of steps
commonly depicted in textbooks as the scientific method." It is much more
than just "doing experiments," and it is not confined to laboratories. More
imagination and inventiveness are involved in scientific inquiry than many
people realize, yet sooner or later strict logic and empirical evidence must
have their day. Individual investigators working alone sometimes make great
discoveries, but the steady advancement of science depends on the enterprise
as a whole. And so on'
Feyerabend recognizes so many other influences in science progress, as does
Latour. I cannot help but take two admittedly cheap shots: ) What would
Feyerabend say of Latour's `method of analysis'? What would Latour say of
Feyerabend depending so heavily on history? Pluralism better describes the
methods of science than Feyerabends pat phrase. Computational science, as
alluded to by Jay, is making big strides (which as an experimentalist I would
say are essentially theoretical) in what Kaufman and Smarr wish to describe
as a third component of science, joining theory and experiment.
Through my own work in science, funded by AFOSR, ARPA, and industry and
science education work funded by NSF, I recognize public, private and
government interest in shaping the motive of research programmes. But one
should just look at policy level statements such as can be found in
http://www.nsf.gov/sbe/srs/seind96/startse.htm or
http://www.nsf.gov/sbe/srs/ostp/assess/start.htm for good examples of that.
Having BEEN THERE, I find the vicarious views of both Latour and Feyerabend
enlightening, but extremely limited. Thinking back on a personal
experimental finding and what we did to validate it helps me explain the
methods used to examine the external world and the role of artifacts (black
boxes in Latours terms). The story certainly makes an unintended case for
theory laden observations.
As a spectroscopist, the essential artifact I applied is called a Fourier
spectrometer, much like the interferometer that Michelson used to measure the
speed of light at the turn of the century. I used the instrument to make
measurements on light emitted by atoms and molecules of oxygen gas. My data
brought an unexplainable new feature after I had rebuilt much of the
apparatus in solution of other problems (Barowy and Sakai, 1984, 1985). We
ran the experiment more times, with varied conditions - the feature
persisted.
The theoretician we were working with was intrigued, but the appearance of
the new feature could mean there was something wrong with the apparatus that
would affect those features_we really wanted to measure_. So we thought
maybe the problem was the inaccuracy of the bearings in the scan mechanism.
After calculation of that effect, which took a foray into the mathematics of
modeling the effect through Fourier transformation, and comparison to the
spectra, we eliminated the possibility - indeed predicting and finding the
scan error features in a different part of the spectrum and also concluding
from the mathematics that that error would have unmeasurable effect on the
actual features of interest.
Then we pursued detector size as a necessary but problematic condition (the
ideal detector would be infinitesmally small) and pursued an analysis
through the mathematics of convolution - the detector size would affect the
shape of the new feature in a small way, but not its existence. We pursued
random sampling errors as the source and could not solve that problem
analytically, and so were left to a plausibilty argument that this was not
also the cause. But we were always nervous, never having more completely
uncovered that part of the `black box'. In the endeavor to eliminate the
feature as an experimental error we found and eliminated many other potential
problems.
We were left to the conclusion that the feature was probably `real' -- that
is, ascribable to light being emitted from the atoms and molecules we were
studying, and not due to misfunction of the black box, which at this point
seemed even less to us as a black box, but more as a marvelous instrument.
In parallel, the theoretician pursued an explanation and other supporting
evidence for that explanation, which we subsequently published (Barowy, et
al., 1986). It was not for another two years that we actually published our
intended work (Chang et al., 1988).
The bottom line was that `anything' did not go. We could have ignored the
new feature, but it had consequences for the quality of our intended work.
We pursued a plurality of methods in finally arriving at our intended
results, however, and the work was distributed across people, other research
programmes, time and space. We took pains to understand the `black box' and,
as I write this, I fully realize that when one describes a `talented
experimentalist' it is because to him or her, the box is not black, but
transparent in the relation of it's design to the technological knowledge
necessary to build it, and to the consequences for the robustness of the
data.
Finally (whew!) there is the second answer for Eva. How the Scientist
evaluates the status of knowledge of an external world is a central
epistemological issue that scientists (especially experimentalists) confront
daily, on a level of interaction between technological artifact (which is
also part of that world!) and that world, and on a level of social
interaction between scientists. Many, according to AAAS, do not think about
it much, but are very involved in just doing it.
Bill Barowy