friedman at math.ohio-state.edu
Wed May 21 02:37:44 EDT 2003
Reply to Steiner 5/19/03 7:58AM.
>In a previous posting, I suggested that Wittgenstein's work could
>stimulate research in fom in the direction of studying how
>physicists "work around" inconsistent systems. I believe that
>Harvey, who originally requested examples of such stimulation, did
>not reject this idea out of hand. The idea is, not necessary to
>defend LW's specific positions, but to gain insight and new research
>problems in the foundations of mathematics.
I have no idea how one would go about profitably and naturally
"protecting" the "rest" of a formal system from its inconsistencies.
The only thing that comes to mind is this. I know some good examples
of where a sentence A, when added to, say, PA, results in an
inconsistency, but where it is known that any such inconsistency is
So we have PA + A is inconsistent, A is a nice, small, interesting statement.
PA + A is naturally protected from infection simply by length.
One could go further and study the formal system PA + A, beyond what
is known. I.e., beyond the fact that PA + A has no reasonable sized
E.g., one can study the truth and falsity of theorems of PA + A,
where the theorems have reasonable sized proofs.
Of course, A itself is provable in PA + A by a small proof, and A is not true.
But one can study a complexity based issue here - it may be that one
wishes to study theorems of PA + A with short proofs where the
theorems have lower complexity than A.
The spectacular event would be something like this, which obviously
is unrelated to the above.
Take the inconsistent full comprehension axiom scheme, and protect it
by some general logical principle, so that the resulting protected
system is not only consistent, but corresponds to a strong system of
set theory such as ZFC. Good luck.
>Here is another attempt at showing how LW could stimulate research.
>LW, as is well known, rejected logical reductions, for example of
>arithmetic to logic (Frege, Russell). His general objection to this
>had to do with the idea that arithmetic is a practice unto itself,
>and embedding it in something like set theory is like taking a
>block, wrapping it in string, and then claiming that it is "really"
>a sphere. Some of the recent postings about real numbers have a
>Wittgensteinian atmosphere to them. However, I think that core
>mathematicians would have little sympathy for the argument, however
>valid, that real numbers are not "really" Dedekind cuts. (I'm not
>taking sides here, just stating a sociological fact.)
I thought I addressed this issue when I made that posting in response
to Heck. See http://www.cs.nyu.edu/pipermail/fom/2003-May/006536.html
Here what integers, reals, ordered pairs, and a bit more really "are"
is elegantly finessed.
>On the other hand, I think that core mathematicians WOULD have
>sympathy for a Wittgensteinian argument concerning the distinction
>between real analysis and complex analysis. ...
>Every mathematician knows that there is a world of difference
>between real and complex analysis, despite the obvious objection
>from "fom" that they are really the same theory, where you
>inteterpret a complex number as an ordered pair of reals to get
>complex from real analysis. An "elementary" proof of the Prime
>Number Theory is one which avoids characteristic concepts like
>analytic function, analytic continuation. etc., and just does
>"straight analysis of functions of a real variable." Here the
>mathematicians, ironically, would take the "Wittgensteinian"
>position (I'm of course speaking of the later Wittgeinstein) that
>the logicians' hierarchies are too coarse to capture what is really
>going on in mathematics.
This is absolutely correct - about the coarseness. And to do
something serious about this kind of thing would require a very
serious and deep modification of the standard setups in f.o.m.
Here is my view. F.o.m. is a science like all others, in that it
engages in a deep understanding of only limited phenomena. The power
of the science depends partly on focusing on aspects of reality that
i) significant and realistic enough to provide new insight;
ii) not too difficult to deal with that progress is slow,
nonexistent, or uninteresting.
In my opinion, we have come nowhere close to doing more than scratch
the surface to understanding the limited aspects of logical reality
that f.o.m. is dealing with now.
I personally at this point think that mining out what we can do now
about these limited aspects of reality, rather than making major
expansions in the scope of f.o.m., is the best course.
That doesn't mean that I am not in favor of major expansion.
There was a major expansion involved, say, in my invention
(discovery) of RM (reverse mathematics) beyond just seeing what can
be formalized in various obvious fragments of ZFC. RM is only at an
early stage of development, as I want to push it into dealing with
the massive amount of mathematics that lives well below the radar
screen of RCA0. RM is still a very classical matter (i.e., crude)
compared to the kind of things that I think you are talking about,
but RM is still a major deep matter.
The long term effort on finding incompleteness results that involve
only concrete mathematical objects manipulated in standard natural
ways, is another example. After all, from a crude point of view,
since Godel already showed that there are even Diophantine problems
independent of ZFC + "there exists a measurable cardinal", provided
its consistent, then what is there to do? Aren't Diophantine problems
pretty much the most concrete problems mathematicians would work on?
But then you ask: display the Diophantine equation, and also ask if
the Diophantine equation displayed stands out among others as
exceptionally memorable, etc. Well, you can't even start to start to
start to start to begin to think about even displaying it.
So if you want a memorable independent statement, wasn't this done by
Godel and Cohen with CH? So then you ask for naturalness AND
concreteness. That's where I am.
The point is that to do anything really pathbreaking PROPERLY
generally takes at least 50 years, and how many 50 year projects can
one have in f.o.m. at one time? Only a very few.
>I'm not sure how to formulate the problem precisely, but: just as
>fom has so successfully studied the idea of mathematical PROOF,
>AXIOM, etc., is there a way to formalize and study the notion of
>mathematical REASONING, so that--even in a single theory, but surely
>in two different theories, even if of the same logical
>"strength"--we could discuss in a useful way concepts like
>"elementary," "explanatory," etc. I'm aware of literature
>concerning complexity of proof, but am not sure that this literature
>is applicable. At any rate, I would appreciate any enlightenment on
Again, this is a terrific project, and probably needs 50 years to do
PROPERLY. Since there is so much fundamental things to do with the
rather limited upgrade that I have made on the scope of f.o.m., I run
shy of really getting into this.
This is not to say that if I tried and really pushed on it, that I
couldn't get somewhere.
If someone were to do something really interesting along these lines,
and I saw a good next step, I might well jump in.
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