[FOM] Dependence relations in model theory, 1
Harvey Friedman
friedman at math.ohio-state.edu
Mon Jul 21 03:08:53 EDT 2003
Reply to Baldwin, Dependence relations in model theory, July 19, 2003,
at 10:55 AM.
The reply will be in two parts. This is the first part.
Let me say at the outset that I very much appreciate the efforts of
Baldwin in discussing contemporary model theory in such a strategic
manner. Some of the discussion is readily understandable by the
preponderance of FOM subscribers, and I'm sure that is greatly
appreciated.
Part of the reason that I am so happy to see Baldwin making these basic
survey postings is that it gives us an opportunity to perhaps see what
is foundational about some of contemporary model theory, and perhaps
help take some of it in more foundationally motivated directions.
Each of the four traditional branches of mathematical logic have their
roots in the deep and fully foundational developments of obvious great
general intellectual interest that have captured the imagination of
scholars in a great variety of fields, and to some extent, the general
intellectual community. I wrote about some evidence for this by
referring to the list of 20 "great minds of the 20th century" compiled
by Time Life books in 2000, in my posting
http://www.cs.nyu.edu/pipermail/fom/2001-February/004794.html
It was nice to see Simpson refer to this also in his posting Thu Jul
17, 2003 5:34:38 PM.
In that Time Life list, fully 3 of 20 scholars listed were closely
associated with foundations of mathematics. The clearest f.o.m. icons
listed there are of course Kurt Godel and Alan Turing, rather than
Ludwig Wittgenstein, who remains deeply controversial. In any case, a
considerable contingent of philosophers back his presence on the list,
but also a considerable contingent would back Bertrand Russell on this
list instead (I'm a Russell fan).
It is interesting to note that Godel and Turing are also the only
persons on this list of 20 who could reasonably be classified as
mathematicians. Also, only two of them (Einstein and Fermi) can
reasonably be classified as professional physicists.
Note how all four traditional branches of mathematical logic have their
roots in Godel and Turing.
Model Theory. The completeness theorem, which asserts that a set of
sentences in a countable first order language is true in all models if
and only if it is provable in an explicitly given formalism associated
with mathematical practice.
Recursion Theory. The analysis of discrete deterministic algorithms via
abstract machines.
Set Theory. If the standard axioms for set theory are consistent, then
they remain consistent if the axiom of choice (and the continuum
hypothesis) is added .
Proof Theory. No consistent suitably axiomatized first order system is
complete, or can even prove (any suitable formalization of) its own
consistency.
There are a few other events in the 20th century in f.o.m. of perhaps a
similar kind of great general intellectual interest than these events,
but the list is not long. Also, the confidence that we have in the
great importance of most of these events is made clearer by further
associated developments, also of general intellectual interest, which
serve to establish the robustness of the notions involved.
I could considerably elaborate on this spectacularly successful story
of the foundations of mathematics in these general intellectual terms,
but this is not the purpose of this posting.
When you reflect on such events, you see clearly how most people with
substantial theoretical scientific instincts or philosophical instincts
- and many people with strong general intellectual instincts - are
moved. Surely for many such people, considerably more has to be said
than these brief accounts above. Sometimes a major gap has to be filled
in connection with many people's lack of familiarity with the general
logical structure of mathematics. But this is generally not difficult
to fill. Of course, sometimes one runs into professional mathematicians
who are particularly uncomfortable with the very idea that there exists
a mathematical subject of such great general intellectual interest and
power (foundations of mathematics) that their mathematical knowledge
and mathematical methods do not seem to illuminate. Such professionals
sometimes have a tendency to dismiss f.o.m. as fruitless third rate
mathematics that should not be pursued in a good mathematics
department. Even these professionals can be turned around if one can
establish an appropriate person to person interaction.
To give a startling indication of how unexpectedly striking f.o.m. is
to a well known applied mathematician/historian, see
Mathematical Thought from Ancient to Modern Times, by Morris Kline,
Oxford University Press, 1972, 1238 pages.
This book ends with Chapter 51, The Foundations of Mathematics. I quote
the first paragraph:
"By far the most profound activity of twentieth-century mathematics has
been the research on the foundations. The problems thrust upon the
mathematicians, and others that they voluntarily assumed, concern not
only the nature of mathematics but the validity of deductive
mathematics."
Again, this is yet more evidence of the great general intellectual
interest of foundations of mathematics, when one considers that this is
written by an applied mathematician/historian who never worked in
foundations of mathematics.
So in deference to this fantastic legacy that affects us all on the FOM
list, that propels foundations of mathematics at its heights to levels
of general intellectual interest that are only matched by the greatest
of all intellectual achievements of the 20th century, we should not use
the term "foundational" lightly. When using this term, we need to keep
this legacy clearly in mind.
If one is to think of some development as "foundational", one should
apply the standards that are appropriate in light of this legacy. This
usually means that the particular recent advance that is regarded as
"foundational" has at least the potential of some substantial general
intellectual interest, but falls quite short of this standard when
examined objectively keeping the legacy in mind. One generally has to
follow up intensively on the advance, in order to bring out the
"foundational" aspects. This generally requires a great deal of
"foundational" imagination, and a clear sense of just what constitutes
general intellectual interest.
Unfortunately, this is not what is normally done. Some advance is made
that has some sort of "foundational" component, generally quite
undeveloped and rough at the edges, and one goes on to further
developments for much more ordinary - but perhaps valuable - purposes.
One generally does not dwell on the truly foundational aspect, and use
it to drive further developments.
This dwelling on the foundational aspect and using it to drive further
developments is absolutely essential to create something of truly
general intellectual interest. In particular, looking back at a series
of mathematically rich developments, however mathematically
interesting, and using the word "foundational" to describe the context,
is not appropriate in light of our fantastic legacy.
It is obvious that model theory, and for that matter, all four of the
traditional areas of mathematical logic, have substantially strayed
away from their roots in foundations of mathematics. To a certain
extent, I believe that this was appropriate and even necessary, in
order to build up the mathematical technology needed for serious
advances in the foundations of mathematics, of general intellectual
interest.
I am optimistic about using this advanced mathematical technology in
order to make such advances. Two approaches to f.o.m. are to
i) revisit various topics that have at least some semblance of a
"foundational" nature and focus on that "foundational" aspect and
rethink the topic in "foundational" terms in order to build the topics
up into something truly foundational, of general intellectual interest.
Of course, my usual approach is to
ii) simply start with the most overarching foundational issues of
obvious general intellectual interest, and develop things from there,
using whatever mathematical tools are available, and trying to invent
whatever mathematical tools are needed.
My keen interest in seeing such valuable postings as Baldwin's and
others, is in connection with approach i).
Harvey Friedman
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