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Harvey Friedman vcinc at
Thu Sep 25 19:38:51 EDT 1997

*temporarily, please address all replies to friedman at
instead of using the reply key*

I have added Barry Mazur to the list, in light of his continued interest in
Reverse Mathematics (and applied model theory), and Wilfrid Schmid to the
list, in light of his continued interest in applied model theory. 

Anand - please continue this correspondence. There is no need for you to
feel that you have to match my responses in terms of the number of bytes. A
brief response or a long response would be appreciated.

Lou - would be nice to hear from you.

>Let me make a couple of maybe overly polemical comments:
>1)  The development of Foundations of Math (Frege-Russel-Hilbert-Godel...)
>was closely related to foundational problems coming out of the math. of the
>time and in particular to the figure of Hilbert, and this gave it its life.
>Current work on Foundations should similarly be informed by the mathematics
>of today, although not in a dogmatic fashion.

a) recall that almost nothing was accomplished in logic and the foundations
of mathematics from the birth of Christ to about 1850 or 1900. The
foundations of thought - which is more general than the foundations of
mathematics - really got going with the work of Frege, as was an essential
development for related and subsequent developments in the foundations of
mathematics. This is before Hilbert. And all applied model theorists use
Frege's work on the foundations of thought (predicate calculus) all of the
time. Lou likes this point.

b) because of the enormous time gap between developments in mathematics and
in the foundations of mathematics - just look at all of that important
mathematics done between the birth of Christ to about 1850 to 1900 - one
cannot even begin to expect that one has even begun to mine out the
significant features of even very classical mathematics with regard to
foundations. More about this below.

c) more or less the same mathematics continues to be taught and required
decade after decade in the undergraduate and graduate mathematics
curriculum. We continue to teach and require these icons of classical
mathematics, that are clearly of a different, more elementary style than a
lot of contemporary mathematics publications - especially in that they are
more general. I am referring to such mainstays of the graduate curriculum as 

"every field as a unique algebraic closure," "the Stone-Wierstrass theorem,"
"every continuous function on a compact set is uniformly continuous,"
"compact = closed and bounded," "the intermediate value theorem," "the
maximum value theorem," "the mean value theorem," "every monotone function
is differentiable almost everywhere," "ordered fields = real fields", "every
real closed field has a unique real closure," "every real closed field
becomes algebraically closed when i is adjoined," "the Cauchy-Peano theorem
for differential equations," "the Hilbert basis theorem," "the Hahn-Banach
theorem," "the Radon-Nikodym theorem," "the closed graph theorem," the Baire
category theorem," "the Lebesgue convergence theorems," "the Riesz
representation theorem," the Riemann mapping theorem," "Fubini's theorem,"
"Fourier transform theorems," "power series development of analytic
functions," "Cauchy's integration theorem," "zeros of analytic functions and
omission of values," "the open mapping theorem," "the maximum modulus
theorem," "analytic continuation theorems", "the Mittag-Leffler theorem,"
"the monodromy theorem," "the no-retraction theorem," "the Picard theorem,"
theorems of Paley and Weiner," "Mergelyan's theorem," "the Brouwer fixed
point theorem," "the Schoenflies theorem," "Sylow theorems," "Ulm's theorem
on Abelian p-groups," "decomposition theorem for Abelian groups," "subgroups
of free groups are free," "power series are Noetherian," "Hilbert's
Nullstellensatz," "Sturm's theorem," "volumes stretched by absolute value of
determinant," "Cayley's theorem," "theorem on symmetric polynomials,"
"fundamental theorem of Galois theory," "unsolvability by radicals,"
"Frobenius and Wedderburn theorems on associative division algebras,"
"Zorn's lemma," "the Jordan-Holder theorem," "the Krull-Schmidt theorem,"
"invariance of dimensionality," "the Wedderburn-Artin theorem for simple
rings," "density theorems for rings," "Artin-Rees and the Krull intersection
theorem," "Artin's solution to Hilbert's seventeenth problem," "metrization
theorems," "simplicial approximation theorem," "Jordan curve theorem," "the
Euler-Poincare formula," "the contraction mapping theorem," "the excision
theorem," "exactness of Mayer-Vietoris," "Jordan-Brouwer separation
theorem," "implicit and inverse function theorems," "Tietze's extension
theorem," "Urysohn's theorem on normality," "Stone-Cech compatification,"
"Borsuk's Antipodal theorem," "Borsuk's separation theorem," "Brouwer domain
invariance theorem," "the Hurewicz uniformization theorem," "fundamental
theorem of the local theory of curves," "the isoperimetric inequality," "the
four-vertex theorem," "the Cauchy-Crofton formula," "Gauss' theorema
egregium," "Gauss-Bonnett theorem," "triangulation theorems," "Poincare's
theorem on indices of a vector field," "the Hopf-Rinow theorem," "the
Hadamard theorems," "Fenchel's theorem," "the Farey-Milnor theorem,"
"Jacobi's theorems on geodesics," "Hilbert's theorem on constant negative
curvature," "Dirichlet's theorem on primes," "the fundamental theorem of
arithmetic," "Minkowski's area theorem," "Chinese remainder theorem,"
"Gauss' law of reciprocity," "Fermat's and Wilson's theorem," "transcendence
of e and pi, and criteria," "various Diophantine equations," "Mobius
inversion formula," "the prime number theorem," Lagrange's four square
theorem," "Hilbert's theorem on sums of k-th powers," "Bertrand's
postulate," "Minkowski's theorem," "Kronecker's theorem on approximations,"

where I only quit because I got sick and tired of compiling this. These
approx. 75 theorems are about 5% of what I have in mind.

d) whereas it is important for foundations of mathematics to bear on
foundational issues that arise from even the most contemporary of
mathematics, foundations of mathematics should, just like mathematics, have
a systematic development. It would be totally absurd not to have as complete
a treatment as possible of the logic of all of the above theorems plus the
remaining 95% of the classical elementary theorems. Please reread a) and b).

e) the current conception of what foundations of mathematics means with
regard to this classical elementary material above (and the other 95% of it)
is focused on rather sharp "quantitative" information - not fuzzy, feely
stuff. It is not focused on the development of tools for generalizations,
sharper results, new proofs, etcetera. Although sometimes these things do
fall out. But it hasn't been the emphasis. This "quantitative" information
is usually in the form of numerical bounds (upper and lower) and above all
what axioms are needed to prove what theorems.

f) this latter preoccupation, "what axioms are needed to prove it?,"
initially had a fuzzy, feely aroma to it until it became clear, through
Reverse Mathematics, that this question surpisingly often has an extremely
precise answer. And, very importantly, one has the following pervasive
phenomenon, which admittedly has to be enlarged and expanded and amplified
so as to attain broader scope:

g) that the formal systems used in this kind of foundations of mathematics
are unexpectedly small in number and usually linearly ordered; and that when
they are not linearly ordered, they are linearly ordered under
interpretability. There has not been any breakage of linear order under
interpretability in a natural context, at least with regard to systems
subject to Godel phenomena. This startling regularity, that these formal
systems seem to represent something completely canonical(!), is what drives
the excitement over Reverse Mathematics.  
******h) we now know of a body of theorems in finite graph theory whose only
proofs at the moment use large cardinals (way beyond ZFC), but which are
considered interesting and relevant to a growing community of discrete
mathematicians and computer scientists. They plan to write about them within
the next few months. Some of these results are now known to require large
cardinals. With regard to your comment about "mathematics of today," some of
these were done by a discrete mathematician in September of 1997. Is that
recent enough?*******  

i) Simpson has made a real dent in the classical elementary theorems that
are still the mainstay of the graduate curriculum, but has a huge way to go.
Reverse mathematics is based on the base theory RCA_0, which is too big to
treat many of these theorems - because they are already outright provable in
RCA_0. Simpson and I have been discussing the second stage of reverse math -
where the base theory is dropped somewhat. It should be dropped only a
little bit at first, in order to get clear about the landscape.  
>2) There has been enormous abstract development of math in past 60-70
>years. Some of these developments can also be considered "foundational" in
>the same way as Cartesian geometry was; for example, the penetration of
>cohomology into many areas of pure math., the Weil conjectures, various
>Lang conjectures (stating amazing conjectural relationships between
>geometry and arithmetic),..... 

I have been acquainted somewhat with this kind of idea. You are hinting at a
conception of "foundations of mathematics" that is quite different in detail
than the usual classical foundations of mathematics. I am extremely
interested in this, especially if it can go beyond the fuzzy, feely stuff. 

The phrase "foundations" has come to mean something moderately definite in
mathematics, statistics, probability, psychology, physics, mechanics,
computer science, economics, finance, philosophy, biology, law, etcetera. I
don't really know how your concept of "foundations" relates to these, where
the emphasis is in the discovery and delineation of concepts, new
definitions that clarify old concepts, the elucidation of basic laws about
fundamental concepts, the derivation of some principles from more
"fundamental" principles, and discussion of nonderivability.  

I certainly believe that there are probably important alternative
conceptions of "foundations" and I would love to participate in their
initiation and development. However, I would like to see some definite ideas
and goals. I would like to emphasize that the present conception of
"foundations" that I work in has a sharp "quantitative" aspect, with clearly
stated goals. I prefer this to touchy, feely stuff. I'd like to hear more
about your vision, particularly if it can be made "hard."

E.g., Lou and I have discussed "what is a good formal system (not subject to
Godel phenomena), and how much math can be done in good formal systems?" and
see some obvious problems in answering this in a suitably convincing way. I
am also interested in "what is the most interesting and elementary
mathematics that cannot be done in a good formal system? i.e., what is
intrinsically bad?"

>One has the feeling that we should make the
>effort to have a "position" on these and other developments, and see to
>what extent the amazing techical development of different parts of math.
>logic can be relevant. (Of course there is a long tradition in logic of
>doing exactly this.)

This sounds like a reasonable general goal for the applied model theory
community that has been, to some extent, followed. Are the applied model
theorists ready to write some visionary articles about this that can be
understood by everyone? Perhaps you can clearly pose a program that many
people in logic could understand and contribute towards. You should
miminimize the technical prerequisites as much as possible in order to make
it palatable to a wide audience. You may have to distill the issues down to
their essence more than you are accustomed to doing.

Of course, one program that I am completely aware of is to find more and
more interesting and strong decision procedures for more and more
mathematics. E.g., Lou did this for the ring of algebraic integers. But a
lot more of this seems likely. However, I don't think that this is what you
mainly have in mind. 

I am of course a little familiar with some classical things; e.g., the
amazing use of complex variables in number theory. Why does it work so well?
Do the applied model theorists know?

>3) For better or worse the "axiomatic" paradigm of math. activity (i.e.
>considering mathematics as the derivation of theorems from axioms) is now
>out of fashion. 

This is much too vague. Let me restate it so that it makes sense and more
clearly reflects the ordinary mathematicians thinking today:

"For better or worse, mathematicians don't pay any attention to what axioms
they use when they prove theorems. This is because they never see any reason
to do so. In fact, there are no foundational problems, since the axioms that
they use represent some infinitesmial fragment of axioms that have long ago
been formulated, studied, analyzed, accepted, given the stamp of approval,
and forgotten. Mathematicians have no problems, and axioms don't help them."

Anand, now that we have growing mounting evidence of steadily higher and
higher quality that this is false on several fronts, how do we educate the

>It is worth trying to understand why these changes of
>fashion come about and how serious they are, as they impact strongly on
>logic. Similarly for other changes of taste, such as the down-grading of
>general topology compared to algebraic and geometric topology.

a) the above situation came about because it took a very very long time for
logic to get enough machinery under its belt in order to get results of
certain kinds. Logic needs even more machinery and development to get even
bigger results of this kind. I have no doubt that the results will be found.

b) general topology continued and died out in favor of algebraic and
geometric topology in the same way that, say, recursion theory continued and
is dying out in favor of complexity theory: 

        i) there was general agreement over a period of time that the
original classical purposes of topology - the analysis and classification of
familiar shapes - was no longer be served by general topology, and
furthermore, the general topologists could no longer say what other
intrinsically interesting intellectual goal is instead being served;
        ii) some gifted people did something about it by proving some
startling and relevant things that did bear on the analysis and
classification of familiar shapes;
        iii) people outside of topology took their responsibilities
seriously and started to support algebraic and geometric topology more
strongly than general topology.

c) there is no doubt in my mind that we will see the same for typical
mathematical logic scence versus foundations; i.e., in the future:

        i) there was general agreement over a period of time that the
original classical purposes of foundations of mathematics - the analysis of
mathematical concepts and reasoning - was no longer be served by work in
typical mathematical logic, and furthermore, the typical mathematical
logicians could no longer say what other intrinsically interesting
intellectual goal is instead being served;
        ii) some gifted people did something about it by proving some
startling and relevant things that did bear on the analysis of mathematical
concepts and reasoning; 
        iii) people outside of typical mathematical logic took their
responsibilities seriously and started to support foundations of mathematics
more strongly than work in typical mathematical logic. 

d) or abstract model theory versus applied model theory:

        i) there was general agreement over a period of time that the
original classical purposes of model theory - the proper analysis and
generalization of algebraic concepts and reasoning - was no longer be served
by work in abstract model theory, and furthermore, the abstract model
theorists could no longer say what other mathematically relevant goal is
instead being served;
        ii) some gifted people did something about it by proving some
startling and relevant things that did bear on the proper analysis and
generalization of algebraic concepts and reasoning; 
        iii) people outside of abstract model theory took their
responsibilities seriously and started to support applied model theory more
strongly than work in abstract model theory. - HMF       

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