FOM: Re: V=L vs. PD
friedman at math.ohio-state.edu
Sat May 13 23:37:10 EDT 2000
Reply to Steel Fri, 12 May 2000 14:55.
>I still don't know whether I'm arguing with Harvey, or with the "normal
I'm not sure you want to argue with either. The normal mathematician, as I
explained in some detail, including my last posting of 1:17PM 5/13/00, is
not at all concerned with mathematics in anything like full generality, and
would very much like to avoid reconsidering axioms and other foundational
issues if at all possible. In particular, that is why they do not react to
the set theoretic independence results with any interest in looking at the
axioms or other foundational issues - because they view this as relevant
only for mathematics concerned with full generality, and they distinctly
are not concerned with full generality.
>My impression from Harvey's post is
>that the normal mathematician, whoever he is, is a small-minded
>character interested in nothing but his own work, who hasn't thought much
>at all about what we want out of our axioms.
The normal mathematician is deliberately completely uninterested in
foundational issues of the sort we are talking about, because they think
that it is only relevant for mathematics concerned with full generality.
>In particular, he doesn't
>realize that the axioms are there to make mathematical work possible, not
>to force work of some kind or other to be done.
The normal mathematician is aware that there are axioms for mathematics
that he is constantly using, but does not recall what they are, nor ever
had a really good understanding of them in the first place. This is because
the normal mathematician thinks that this has been well worked out by the
early part of the 20th century, and there are no issues or difficulties
left relevant to normal mathematics. That if they just proceed according to
their standard intuition, they will work within the usual axioms. That
unless they venture out into mathematics concerned with full generality,
they will never run into any axiomatic problems. This is why they are not
concerned with questions like the continuum hypothesis or the projective
>Perhaps we should spend
>some time trying to enlighten this character, but why should he be the
>focus of this discussion?
Of course, I am spending an entire career aimed at enlightening the normal
mathematician, but this requires appropriate new kinds of results which
have proved very difficult for me to obtain. The normal mathematician has
to be a major focus of mathematical logic not only for political reasons,
but also because the relationship between these two cultures is of
fundamental intellectual importance independently of politics.
>Obviously theories need applications.
The matter of applications is far far more critical than this sentence
suggests in the case of set theory. There are special difficulties with set
theory that are completely uncharacteristic of any special difficulties
encountered in normal mathematics. And these special difficulties are
inexorably intertwined with a nearly universal feeling of suspicion - at
various levels - of set theory. There is a general feeling that, as a
matter of principle, such abstract objects, apparently completely remote
from any arithmetical, algebraic, or geometrical considerations, must be
inherently useless for any arithmetical, algebraic, or geometrical
purposes, including any connections with science and engineering. The
objects of higher set theory are naturally regarded as unnatural foreign
intruders into normal mathematics.
So it is not merely a matter of set theory needing applications. It is a
matter of a deep suspicion that set theory cannot possibly have any
applications - as a matter of principle - except to mathematics (such as
set theory) that is concerned with full generality.
>I have a high opinion of the work
>Harvey has done in applying large cardinal theory. But it is absurd to
>suggest that until this work had been done, it would have been rational to
>reject large cardinal theory, to prohibit or discourage its development.
First of all, this is not just a matter of large cardinal theory. No normal
mathematician has ever really used even a hefty fragment of Zermelo set
theory for any normal mathematics. (This is particularly true if we are
talking at the level of discrete and finite mathematics). There is the deep
suspicion even that set theory at the level of a few iterations of the
power set over omega is completely worthless for normal mathematics.
So the issue is not really large cardinals. The issue is whether
substantial set theory well within ZFC has any significance for normal
mathematics. I could even make the point incomparably stronger - what about
the higher reaches of Z_2?
It turns out that Boolean relation theory promises to be by far the most
convincing way we know of at the moment for dealing with the crucial issue
even at the level of Z_2 - despite the fact that it actually deals equally
well with the issue at the far far far higher level of small large
cardinals!!! (As I have said earlier, I am expecting extensions of Boolean
relation theory to deal properly with the entire large cardinal hierarchy
through j:V into V).
Secondly, I am not saying that it would have been rational to reject large
cardinal theory, or Zermelo set theory, or ZFC, until something like
Boolean relation theory is done.
What I am criticizing is the lack of identification as to what the really
crucial issue for large cardinals - or set theory for that matter - has
been. The set theory community has consistently acted like this was not the
major crucial issue. Instead the idea was promulgated that the issue of
just what good set theory is for anything has already been fully resolved
for all significant parties by determinacy, starting at the Borel level.
In particular, recognition of the crucial issue cannot be found in the set
theory community either in choice of research programs, choice of thesis
topics, discussions at meetings, invitees to meetings, or short term and
long term hiring.
>Harvey's own work would never have been done in that case.
>would never have been discovered by looking through the lens of Boolean
The first sentence here is false or at best very misleading. The hierarchy
of Mahlo cardinals that figures so prominently in Boolean relation theory
and earlier work of mine, was invented by Mahlo in a series of papers in
1911, 1912, 1913. Steel can hardly be referring to prohibiing or
discouraging this work of Mahlo in the years 1911, 1912, 1913. At that
early time, there was hardly anything around to prohibit or discourage. And
let me just say that if Mahlo did this in 1911 - 1913, then any of a number
of people - including me - could have been expected to do this by the year
2000. And, of course, only basic elementary work is needed for Boolean
relation theory in connection with Mahlo cardinals. I certainly have known
about Schmerl's Ph.D. thesis in the 1970's with Jack Silver about the
Ramsey theoretic aspects of the Mahlo cardinal hierarchy. But again, the
relevant part of his work lies within the range of many people after the
Mahlo hierarchy is set up and one wants to do the combinatorics of Mahlo
Also, as indicated above, something like Boolean relation theory is
absolutely crucial to find even at the level of ZFC and far below. Here
there are no large cardinals involved.
>Large cardinal hypotheses flow from general foundational
Absolutely true, but even here I have a sharp disagreement with the set
theory community. They have not recognized the need for, and the realistic
possibilities of, obtaining far better intrinsic justifications for even
small large cardinals than we have today. In fact, we need, and ought to
look for, deeper intrinsic justifications even at the levels of ZFC and
Zermelo. Flow is not enough.
>and by developing the extensive theory around them in a
>natural way, we only make important applications more likely.
This may make sense in theory but not in practice. The intense development
of the extensive theory surrounding them accompanied with the de-emphasis
of the crucial issues, has these potentially negative effects:
1. It diverts valuable resources needed for dealing with the crucial issues.
2. It pushes students away from dealing with the crucial issues in their
theses and later in their careers. Once committed to and rewarded for work
done in the "extensive theory", experience shows time and time again that
they will continue to ignore the crucial issues for their entire career.
3. It gives the normal mathematical community the impression that it is an
intricate but isolated area about which their suspicions are confirmed -
that it is intrinsically useless for anything other than mathematics
concerned with full generality.
4. It discourages people from pursuing the crucial issues in the following
sense. Such work would normally have to be judged by the set theory
community. The set theory community, being preoccupied with the "extensive
theory" rather than the crucial issues, would not support such research at
anything like the level of support they give of work in their favorite
"extensive theory" - at least not until very very late stages of such
research. Hence anybody pursuing the crucial issues is not going to get any
kind of proportionate positive feedback for doing so. So if it is a
difficult process taking several decades to reach full fruition, and if the
principal specialists are reserving their positive feedback for the
"extensive theory" then who in their right mind would pursue the crucial
issues with anything like the effort that is needed? Absolutely no normal
The way to make "important applications" more likely - I would rather say
"progress on the crucial issues" more likely - is to
a. Teach your students what the crucial issues are. (The generic "you" -
not particularly Steel).
b. Encourage your students to get involved in the crucial issues. (The
generic "you" - not particularly Steel).
c. Think about the crucial issues. (The generic "you" - not particularly
d. Support people who propose to pursue the crucial issues and/or succeed
with the crucial issues the same way that you support people who propose to
pursue the crucial issues and/or succeed with the "extensive theory." (The
generic "you" - not particularly Steel).
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