Marker/Simpson correspondence on foundations
Stephen G Simpson
simpson at math.psu.edu
Thu Sep 25 21:33:05 EDT 1997
OK everybody, here is the famous or infamous Marker/Simpson
correspondence. In part it is a discussion of the significance of
recent research on the incompleteness phenomenon and applied model
theory. There is also a discussion of broader issues: what is
foundations of mathematics, should mathematicians be interested in
foundations, technique versus subject matter, etc.
A couple of comments about this Marker/Simpson correspondence:
1. It took place in December 1995 -- a lot longer ago than I had
thought! Time flies.
2. These are unedited e-mail messages rather than well thought out and
edited opinion papers; also, they were written in 1995, before Harvey
circulated his long-awaited manuscript in summer 1996.
-- Steve Simpson
From: Stephen G Simpson <simpson>
To: marker at math.uic.edu
Cc: InstantP at aol.com (Harvey)
Date: Sun, 3 Dec 1995 11:28:11 -0500
How are things? I'm glad that your research is going well, etc.
Harvey Friedman phoned me yesterday saying he had talked with you
about Angus Macintyre's views on the
Frege-Russell-Hilbert-Gödel-... line of research in foundations of
mathematics. According to Harvey, Angus gave a talk at a meeting in
Italy expressing a rather low opinion of this line of research.
There may have been some influence from Kreisel.
As you know, Harvey and I think highly of the Hilbert-Gödel line and
consider ourselves to be carrying it on. So, naturally, we'd like to
learn more details about the views of Angus and those in his circle.
Would you be able to point me to some published material on this? For
instance, the text of Angus's talk in Italy would be of interest.
(I'm sorry I don't have more information about the time and place of
the talk.) If you give me Angus's email address, I'll ask Angus
Harvey and I are thinking of possibly writing some kind of position
paper about technical work in mathematical logic, recursive function
theory, etc. and its relation to foundations of mathematics.
-- Steve Simpson
Stephen G. Simpson
Department of Mathematics, Pennsylvania State University
333 McAllister Building, University Park, State College PA 16802
Office 814-863-0775 Fax 814-865-3735
Email simpson at math.psu.edu Home 814-238-2274
World Wide Web http://www.math.psu.edu/simpson/
From: marker at math.uic.edu
To: simpson at math.psu.edu
Subject: Re: hi
Date: Mon, 4 Dec 1995 10:25:27 -0600
Angus' e-mail address is ajm at maths.oxford.ac.uk
He is currently in the middle of a five year fellowship from the
Science and Research Council and frequently away from Oxford, but
usually is in a position to read his mail.
I am affraid I do not know what Angus said at the meeting in
Sicily, indeed Harvey is the only person who has mentioned it to me.
(There was a meeting in Sicily in early September with a number of
philosphers, logicians and other mathematicians (Manin is the one
I remember) on "Truth and Mathematics").
I think it would be presumptuous of me to speak for Angus, but I can
try to quickly summarize some of my own ideas (I should appolovize
here as I am logged in from home and have very little to edit or correct
as I go).
-"Foundations of Mathematics" is a subject somewhere between mathematics
and philosophy. What is it relevance for mathematicians? Certainly
Godel's theorem is one of the most significant intelectual results of
our century and every mathematician must be aware that formal methods
are necessicarily incomplete. But how does this influence the practice
of mathematics? Certainly this has a large impact on any mathematical
subject that studies arbitrary uncountable structures (general topology,
large abelian groups...) Any researcher in this area must be aware of
incompleteness phenomena and set theoretic methods. (Of course this
type of phenomena have only appeared in the fringes of the subject.)
On an intelecutal level I find the calibration of interesting
mathematical phenomena with set theoretic principles quite interesting.
Harvey's old results on Borel determinacy is one of my favorites and
I have a great deal of respect for the current CABAL program calibrating
determinacy with large cardinals and inner models.
I just don't think these results have a great deal of influence on mathematical
practice. [Perhaps they do in the following sense: earlier I dismissed
general topology, for example, as a "fringe area", perhaps a good working
test for a fringe area is one where set theoretic methods have taken over]
-I must say that I am not particularly taken with Harvey's program of the
last decade or so, for, while I don't think I can articluate whet the
difference is, there is a large difference between "looking natural" and
"being natural". I find the "Borel diagonalation" results of 15 years ago
-The Shelah program in model theory was an attempt at a different
kind of "Foundations". It was an attempt to build an abstract theory
of mathematical structures. Over the past ten years the prevailing
philosophy of model theorists has changed and is much more in line with the
thinking of Macintyre, van den Dries and Wilkie. Now the main idea is to
try to use logical tools to analyze concrete mathematical structures.
This has led to two major successes; the breakthroughs on exponentiation
in real analytic geometry and Hrushovski's proof of the Mordell-Lang
conjecture for function fields. (An interesting point is that while
the work on exponentiation uses only Robinson style model theory,
Hrushovski's work uses a great deal of both classical stability theory and
the more recent geometric theory).
-I, at first, considered the Hrushovski-Zilber work on Zariski geometries
to be an important step in a different kind of foundations of amathematics.
(This will appear in Jour AMS, but an extended abstract appeared a couple
of years ago in the Bull AMS). They gave some simple properties of a
toplogical space, from which one could deduce the presence of an interpretable
algebraically closed field so that the space was the Zariski topology of
the curve over the field.
A year later these ideas ended up being central to Hrushovksi's proof of
I apologize again for the sloppy typing.
I hope these comments are somewhat helpful though they do represent my
From: Stephen G Simpson <simpson>
To: marker at math.uic.edu
Subject: fringe mathematics
Date: Wed, 6 Dec 1995 18:16:15 -0500
Thanks for your letter. I'll try to find out from Angus exactly
what he said at the meeting in Sicily.
> Godel's theorem is one of the most significant intelectual results of
> our century and every mathematician must be aware that formal methods
> are necessicarily incomplete. But how does this influence the practice
> of mathematics? Certainly this has a large impact on any mathematical
> subject that studies arbitrary uncountable structures (general topology,
> large abelian groups...) Any researcher in this area must be aware of
> incompleteness phenomena and set theoretic methods. (Of course this
> type of phenomena have only appeared in the fringes of the subject.)
Harvey is showing that incompleteness phenomena apply also to
non-fringe mathematics. If he can do that, it's very interesting,
wouldn't you agree? It should be interesting not only to some or all
mathematicians, but also of general intellectual interest.
Are you familiar with the Friedman-Robertson-Seymour theorem showing
that the strength of the graph minor theorem is greater than Pi^1_1
comprehension? The graph minor theorem is hardly fringe mathematics.
> perhaps a good working test for a fringe area is one where
> set theoretic methods have taken over]
Yes, I see what you mean. It's remarkable the way mathematicians
often tune out whenever set theoretic methods come in.
But I can't accept your statement about fringe areas. Taken
literally, it would seem to imply that the interest of a subject
matter is to be judged in terms of the methods used to study it.
Intellectually, I can't accept this criterion. We have to keep
methods in their place. Methods are only a means to an end, not an
end in themselves. There is such a thing as intrinsic intellectual
interest of a subject matter, independently of the methods used to
study it. If ugly methods are used to prove an incisive theorem that
is illuminating or beautiful or of great practical importance, one
would not for that reason run down the theorem or the subject matter.
> -I must say that I am not particularly taken with Harvey's program
> of the last decade or so,
I'm not sure what you mean. During that decade he obtained a lot of
results that I don't think you are very familiar with. (Hardly
anybody is, because he has published very little of it.) I think it's
quite possible that his most recent formulations will knock your socks
> -The Shelah program in model theory was an attempt at a different
> kind of "Foundations". It was an attempt to build an abstract theory
> of mathematical structures.
I don't see how Shelah classification theory has anything to do with
the Frege-Russel-Hilbert-Gödel-... line that we are discussing. In
the F-R-H-G line, we are trying to formalize mathematical practice and
study properties and limitations of such formalization. Shelah-style
classification of arbitrary mathematical structures is a far cry from
that. The only connection I can see is that both use the technical
notions of "first-order formula" and "satisfaction".
> Now the main idea is to try to use logical tools to analyze
> concrete mathematical structures.
Well, if analysis of concrete mathematical structures is the goal,
then there is no intellectually sound reason to limit yourself to
logical tools. Intellectually, the right thing to do would be to use
all available tools (insofar as they are useful). This assumes of
course that the your concrete mathematical structures are of interest
apart from the tools. (If they aren't, then you are talking about
literally "technical" research, technical in the sense of focusing on
techniques rather than subject matter or results. Technical research
in this sense can be interesting, but it shouldn't be, and usually
isn't, regarded as high-level stuff.)
I think you can see where this leads. If you regard, say, Zariski
geometries as intrinsically interesting, then you should want to use
all available tools to study Zariski geometries. But then, how are
you different from a geometer? There's nothing wrong with being a
geometer, but it has less and less to do with foundations. (Or, same
question replacing Zariski geometries by function fields and
"geometer" by "algebraist".)
Sorry to have gotten a bit polemical here, but these things are
important to me.
From: marker at math.uic.edu
To: simpson at math.psu.edu
Date: Thu, 7 Dec 1995 21:35:03 -0600
Let me make some comments on your last note. First, let me say that
I hope you in no way take my comments as being desparaging of
Harvey's work or your work. I have a great deal of respect
for both you.
-My comments on "fringe mathematics" were intended to be somewhat
glib. The central questions in group theory are about finite groups,
some countable groups and Lie groups. These are the questions which
have a baring on problems in number theory, dynamical systems and
physics. Similarly, the important problems in topology are about
smooth manifolds of reasonably low dimensions. While researchers
continue working on more abstract problems about abstract uncountable
groups and topological spaces, these are far from central areas of
mathematics. (You and Harvey should not find this too controversial as
this is one of the main points behind Harvey's Borel Model theory).
Moreover it is no longer suprising (either to logicians, practioners
in these areas or other mathematicians) to find independence phenomena
in these areas.
Certainly I do not believe that the importance of a subject
is derived from the methods used. Indeed, the usefulness of
model theoretic methods in classical mathematics is my main interest
at this point in time.
-I think that the main point of the reverse
mathematics program is that there are five fragments of second order
arithmetic that suffice to classify the strength of most theorems of
classical countable and continuous mathematics. This is without doubt
an important and intriguing point. But does this in anyway effect
mathematical practice? (this is perhaps related to the
To answer your question I don't consider
the Seymour-Robinson theorem as a "fringe" result (nor do I consider
it "central"). I think that the result that this requires long
iteration of hyperjumps a very interesting result from a technical
point of view and the fact that this is one of the few natural
results which goes beyond the basic five systems is also of great
interest...from a metamathematical point of view. But does this fact
influence the practice of graph theory (of course it might have if,
like Borel determinacy, the reverse direction was proved first)?
Moreover, I doubt that any graph theorist would even find it
suprising that this difficult result dealing with well
founded parts of relations requires a very good theory of countable
ordinals to prove.
-You are right that I have not seen exact statements from Harvey for
a couple of years (and have not seen even hints of proofs for much
longer). Still I will be very suprised if they knock my socks off.
I suspect that if I every see these arguements I will once again
be impressed with Harvey's insights and technical achievements.
On the other hand I suspect that I will still view this as coding
set theoretic phenomena in a natural looking way and I believe that
there is a big difference between "looking natural" and "being
natural". Also again I ask what does it say about mathematical
practice. We have known that 1-consistency of large cardinals is
an independent arithmetic statement. Now we know that we can code
this up in a cute way, but this will only be truly important if
we such phenomena are found in problems we want the answer to.
(I am ignoring here the rather compelling argument that this
work must be started now so that in a couple of hundred years
when such problems arise, some of the necessary machinery will
-I think I take a broader view of the foundations of mathematics
than you do. I consider as "foundational" any work that sheds light
on mathematical practice and mathematical thinking. I think Shelah
would consider his classification program as foundational in this
sense. To me one of the most important points in the foundations of
mathematics is the duality between algebra and geometry.
While the fact that Desarguesian projective planes can be coordinatized
by division rings is arguably just a theorem of geometry, I think it is
an important foundational result because it clarifies this duality.
The Hrushovski-Zilber result is just as striking (more so perhaps
because the connection between topology and algebra is forged
with highly sophisticated model theoretic machinery).
Of course the beauty of these results is that in addition to their
foundational interest they have proven to be mathematically useful.
-Finally, when I said that my interest was in using logical tools to
study interesting mathematical structures, I mis-stated things abit.
Certainly when I am working on expansions of the reals (or
differential fields) I do not limit myself to logical methods. But
these are just the things I know best. This is I suspect the dividing
line that makes me a logician, instead of a real geometer.
I certainly make no claim of working in foundations.
I hope these comments clarify my opinions.
From: Stephen G Simpson <simpson>
To: marker at math.uic.edu
Subject: foundations, etc.
Date: Thu, 14 Dec 1995 15:53:45 -0500
Again, thanks for your reply. I wrote to Angus but he doesn't seem to
be answering his email. If you can find out more of what he said in
Sicily, or point me to related Macintyre or Kreisel-Macintyre
publications, I'd be most grateful.
> Certainly I do not believe that the importance of a subject
> is derived from the methods used. Indeed, the usefulness of
> model theoretic methods in classical mathematics is my main interest
> at this point in time.
Well, sure, but the question is, which do you regard as key, the
classical mathematics questions, or the model-theoretic methods? If
the former, then progress should be measured by success in answering
those questions, by any and all methods. In other words, if you are
studying classical algebraic questions for their own sake, then you
are competing with algebraists on the basis of results obtained, not
And then there is the deeper question of what wider intellectual
interest is served by classical algebra; most people other than pure
mathematicians regard Gödel's incompleteness theorem as interesting
and algebraic geometry etc as obscure; do you think these people are
Still, I have to say I'm impressed by what Hrushovski and other
applied model theorists (including you, Wilkie, Macintyre, van den
Dries, etc) have done. Tell me, has it reached the point where
algebraic number theorists have to take notice of Hrushovski's
results? Of model-theoretic methods? (These are two distinct
questions, of course.)
> -I think that the main point of the reverse
> mathematics program is that there are five fragments of second order
> arithmetic that suffice to classify the strength of most theorems of
> classical countable and continuous mathematics. This is without doubt
> an important and intriguing point. But does this in anyway effect
> mathematical practice? (this is perhaps related to the
> Kreisel-Macintyre point)
My contributions to reverse mathematics have more of a philosophical
motivation, e.g. what is finitism, what would be the consequences of a
through-going finitist approach to mathematics, etc. I don't expect
this to have much effect in math departments, unless mathematicians in
math departments resume paying attention to philosophical issues. I
think mathematicians should resume paying attention to philosophical
issues, but then again many pure mathematicians are notoriously
narrow-minded, as evidenced by the way they turned their backs on some
of the most interesting parts of mathematics (foundations, complexity
theory, statistics, much of applied math and numerical analysis, etc).
As to the Kreisel-Macintyre point, I don't know what the point is,
since I didn't hear the speech or read the paper, if there is one.
> Moreover, I doubt that any graph theorist would even find it
> suprising that this difficult result dealing with well
> founded parts of relations requires a very good theory of countable
> ordinals to prove.
I don't agree. Most work in this area of graph theory (which
has applications to VLSI design etc) is very finitistic.
> practice. We have known that 1-consistency of large cardinals is
> an independent arithmetic statement. Now we know that we can code
> this up in a cute way, but this will only be truly important if
> we such phenomena are found in problems we want the answer to.
Whe you say "problems we want the answer to,", who is "we"? We
geometers? We algebraists? Most people (other than some pure
mathematicians and, possibly, Kreisel and Macintyre) already regard
Gödel's incompleteness theorems as very interesting and truly
important, even if Gödel's theorems didn't answer a specific question
that they had in mind before hearing of Gödel's theorems.
> -I think I take a broader view of the foundations of mathematics
> than you do. I consider as "foundational" any work that sheds light
> on mathematical practice and mathematical thinking.
This is too broad. Most high-level mathematics has this quality of
shedding light on broad areas of mathematics. That doesn't make it
What I mean by "foundations" (as I defined it at the beginning of this
discussion) is the Frege-Russell-Hilbert-Gödel-... line: formalization
of mathematical practice and the study of properties and limitations
of such formal systems. Hilbert's 2-volume study of this subject was
entitled, appropriately, "Foundations of Mathematics."
> I think Shelah
> would consider his classification program as foundational in this
> sense. To me one of the most important points in the foundations of
> mathematics is the duality between algebra and geometry.
These are interesting lines of mathematical research, but they have
little to do with the FRHG line.
> Certainly when I am working on expansions of the reals (or
> differential fields) I do not limit myself to logical methods. But
> these are just the things I know best. This is I suspect the dividing
> line that makes me a logician, instead of a real geometer.
The fact that someone knows logical methods best does not make him a
logician. By definition, a logician is "one who studies logic" (by
all available methods), not "one who studies geometry (by all
available methods), but who happens to know logical methods best."
Subjects are defined by subject matter, not by methods.
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