FOM: Does Mathematics Need New Axioms?

[Harvey Friedman]

Reply to Steel Wed, 16 Feb 2000 11:29.

I am very pleased that Steel has confirmed that I had stated his views
fairly accurately, for the most part, and that he has taken the time to
clarify and amplify them.

I am in sharp disagreement with him on certain points, so much so that we
are in imminent danger of talking past each other in a panel discussion
format. So I am convinced that that panel discussion will be greatly served
by airing out the differences on the Internet.

In fact, the disagreements over a few points - not the vast majority of
points - are so sharp as to undoubtedly be mostly due to some failures of
communication. Perhaps the use of words, perhaps a misunderstanding of
information that is not publicly available, and the like - which can be
corrected before the public discussion takes place.

>> Steel would emphasize the large cardinal axioms as what he views
>>is the canoncial extension of the usual ZFC axioms, and their productive
>>use in settling problems about the projective sets.
>
>     Yes, for me, and I think many others who have worked in this area,
>these are the main points.

So we agree that these are the main achievments of the set theorists in
large cardinals (including consistency strengths as Steel indicates below).
However, although it appears that the large cardinal axioms are the
canoncial extensions of the usual ZFC axioms, the reasons given leave much
to be desired, even at the level of small large cardinals. This problem of
showing that even the small large cardinals form a canoncial extension of
the usual ZFC axioms seems to me to be of comparable importance to other
issues with regard to large cardinals that are being actively pursued - yet
this issue is not, as far as I know, being addressed by the specialists in
set theory. (Naturally, I wouldn't say this if I didn't have definite ideas
about it).

>I would add that the role of large cardinal
>axioms in calibrating consistency strengths shows how central they are.

I would say that this indicates their importance for abstract set theory.
E.g., it does not show that they are central for mathematical logic as a
whole, and certainly not for mathematics as a whole.

>>In particular, Steel is aware of the disinterest among mathematicians in
>>the continuum hypothesis and the projective hierarchy. But, as opposed to
>>Maddy, for Steel this is not an intellectual matter worthy of research
>>investigation that is to be worked into one's philosophical/mathematical
>>views or one's research.

>   There's no mystery in the fact that number-theorists have no interest,
>qua number-theorist, in large cardinals. For all we know, large cardinals
>might be needed to prove the Riemann Hypothesis, but it would make very
>little sense for anyone working on the RH to look that far afield.

I think you miss my point. Set theorists are far more interested in number
theory than number theorists are in large cardinals and the projective
hierarchy. For instance, topics like "there are infinitely many primes in
every appropriate arithmetic progression", or FLT, or Goldbach's
conjecture, or the prime number theorem, or e+pi is irrational, or
2^sqrt(2) is transcendental, or RH - these are of nearly universal interest
among mathematicians, not just number theorists, even if they are not
familiar with the relevant papers and proofs.

Set theorists do not expect to be able to use such number theory in their
work any more than number theorists except to be able to use modern set
theory in their work. But there is a big difference in the attitudes each
other have towards the other subject.

There is no reason to dwell on number theory or number theorists. Replace
number theory/number theorists with many other branches of mathematics.
E.g., topologists, geometers, mathematical physicists, etcetera.

>   It's important for a theory to have applications, but you can know that
>a theory represents a basic conceptual advance without a long list of
>applications.

The issue with regard to large cardinals is not trying to turn a
substantial list into a long list. The issue is that from the point of view
of mathematics, the list is both tiny and totally unconvincing and
idiosyncratic *to them*. There are systemic problems with this tiny list
that practically scream out to the mathematician that for him that list is
not real - for him that list is the empty list. For him, this is an
irrelevant abstract game that bears no resemblance to any mathematics that
he can touch or feel - certainly none that he could even in principle
encounter in the settings that he is familiar with. That there is an
intrinsic disconnect at the most fundamental level.

Let's compare this with the situation with differential equations. The
origins of differential equations come from physics, so the origin is
practically one big application. So when differential equations develops -
as all subjects do - a theoretical side, independently of applications,
people are not surprised that some of this work finds its way in
applications, or at least is useful for people doing applications. There is
a universal recognition of at least the real possibility of applications
even if the theory gets removed from the applications. They do not dismiss
differential equations - even the abstract parts - as some crazy abstract
game that cannot, in principle, have anything to do with anything that they
can touch or feel.

Whereas here with large caridnals - or even substantial fragments of ZFC -
for most mathematicians, there isn't even the recognition of the
possibility of applications to anything that they would regard as "normal"
mathematics. They could not even imagine this possibility, and so they, at
least at the subconscious level, doubt that it can ever have any
applications to any "normal" mathematics.

>Newton must have known his theory of gravitation was such an
>advance as soon as he had derived Kepler's Laws, if not before.

That was a great application to something real!

>I think we
>know enough about large cardinal axioms and their consequences to see that
>they represent a basic conceptual advance.

Who is "we"? If we is set theorists, then I agree, although I would say
this: set theorists may know that large cardinals represent a basic
conceptual advance, but set theorists don't quite know what that basic
conceptual advance is.

As I have said in other postings, I am convinced that set theory (with
large cardinals) is part of, or falls out of, a wider theory involving more
primitives. When this wider theory is understood, the large cardinal axioms
will drop out as naturally and clearly and compellingly as, say, induction
on the integers. But we are not there yet.

>   The more large cardinals are applied, the more important the advance. I
>greatly admire Harvey's work directed toward finding concrete, natural,
>combinatorial consequences of large cardinal hypotheses.

Thank you very much! I find this half of the paragraph more congenial than
the next half.

>I might point out
>that if this work has long-term significance, then so do large cardinals,
>whereas the converse is not true, and therefore the long-term significance
>of this work is subject to at least as much doubt as is the long-term
>significance of large cardinals.

This is by far the most confusing thing I have ever read by Steel. I
cannnot imagine what Steel has in mind here.

For the purposes of discussion, let us use as a representative of "my work"
the most recent theorem/conjecture/partial conjecture I posted, where I am
just about to claim a somewhat different partial conjecture, and am
hopefully well on track on much stronger partial conjectures.

Let us simplify the conjectures as follows, for the sake of clarity of the
discussion:

CONJ 1: It is necessary and sufficient to use certain small large cardinals
in order to completely analyze the following finite set of problems. The
universal solvability of any given Boolean relation between three infinite
sets of natural numbers and their images under two multivariate functions
on the natural numbers.

CONJ 2: In any instance of such a problem, if one can find arbitrarily
large finite solutions, then one can find infinite solutions.

CONJ 3: In any instance of such a problem, if it is true for functions of 2
variables then it is true for all multivariate functions.

I know (proof needs to be checked carefully) that it is necessary to use
these small large cardinals to prove any of these three conjectures. I
don't know that they are sufficient for any of them. Significant partial
results seem to be coming along fine.

I believe that this universal solvability subject is of immediate,
compelling appeal to a huge range of mathematicians. Theoretically, to the
entire mathematical community - but I have learned over the years that that
is usually too large and diverse a set to quantify over.

In particular, I have some quick feedback that this universal solvability
subject is "completely fundamental and compelling" from, say, a specialist
in several complex variables who knows virtually nothing about mathematical
logic.

Contrary to what Steel says, the long term significance of this work -
assuming the conjectures are proved, or at least sufficiently strong
partial forms are proved - is not dependent on the long term significance
of large cardinals. In fact, the long term significance of this work
(assuming ...) is immediately obvious. Here are the reasons:

1. There are very natural restrictions of these conjectures that are
expected to be equivalent to the 1-consistency of ZFC over ACA. Thus the
long term significance would only therefore depend on the long term
significance of ZFC, which is not dependent on the long term significance
of large cardinals.

2. There are even very natural restrictions that are expected to be
equivalent to the 1-consistency of the theory of types over ACA.

3. Or, for that matter, of most really natural levels <= ZFC.

In fact, from the viewpoint of the history of mathematics as we know it, it
is almost impossible to imagine that any long term significance will be
attributed to large cardinals unless one has a genuine application of them
to what mathematicians feel is "real", and this probably has to be
accompanied by the feeling that it is not an isolated application, and a
proof that the use of the large cardinals is essential.

>>More specifically, Steel views the mathematicians' interest/disinterest
>>or attitudes towards problems and topics in set theory as sociology,
>>which is of significance only in the role that it plays in funding and
>>job opportunities. For Steel, this is something that is subject to
>>unpredictable change and fashion and has no basis in real philosophical
>>or mathematical issues.

>    Actually, these are not my opinions. The number-theorist's disinterest
>in learning large cardinal theory is rational. His unwillingness to hire
>set theorists would be understandable, but not rational.

I never suggested that a number theorist would, rationally, feel compelled
to learn large cardinal theory, or that a set theorist would, rationally,
feel compelled to learn number theory. What I was saying is a lot closer to
your second sentence.

But why is that not rational, if the number theorist's perception is that
large cardinals are a remote game that is in principle impossibly far
removed from what "normal" mathematics is about, when there are many many
job candidates who work directly in "normal" mathematics?

> I think of what
>goes on in hiring committees and funding agencies as applied philosophy of
>mathematics. Of course, fashion plays a role there, but in my experience
>there is a substantial rational core.

You don't agree that the *perceived* fundamental disconnect between
abstract set theory and "normal" mathematics has a major serious negative
impact in the reward system in the U.S. mathematics community? Sure,
nothing is absolutely black and white, and there are certainly some people
who can get around such problems because they have something else to offer.
E.g., local politics of various sorts, or that somebody is the best set
theorist in 1000 years, and the like.

I am confused. If you agree with the previous paragraph, then are you
saying that this is rational or irrational?

>   I would qualify this two ways. First, one needs much more than the
>abstract possibility that large cardinals might someday be useful to
>justify work in the field.

I don't know how this sentence fits exactly into the argument. But let me
respond to it.

Large cardinals already has a lot more going for it than just the abstract
possibility that it might someday say something about a "normal"
mathematical situation - even without my efforts.

However, there the field has a great deal left to be desired both in terms
of philosophical coherence and in terms of saying something about a
"normal" mathematical situation.

>Second, I don't have any objection to informed
>criticism in the proper forum.

I hope that you think this is a proper forum. It is very public, of course.
And I have a rule for myself: I avoid criticizing unless I am proposing a
better alternative. Just criticism in a vacuum, without positive
suggestions - I don't like to see it, and I don't like to do it.

> >It is also my impression that Steel feels that current mainline research
>>in set theory is based on views that are philosophically attractive, but
>>perhaps not fully coherent

>     Yes. Are anyone's views in this arena fully coherent?

The issue for me is to what extent one recognizes the incoherences, and
tries to remedy them. In particular, to what extent does one take into
account the shortcomings in the formulation of research programs? I don't
see very much of this sort of thing in the mathematical logic community.
People get committed and hugely invested in a line of research, and they
don't like to make 90 degree turns very much.

On the other hand, it is not easy for most people to incorporate genuine
philosophical considerations in their research plans. But I feel it is
important to try.

>>, and certainly not explainable in elementary
>>terms that are readily accessible to outsiders, even within the
>>mathematical logic community. But in his view, coherence and
>>explainability should in no way influence the direction and emphasis of
>>research in mainline set theory, nor deter or slow down its intensity. In
>>his view, it is certainly not appropriate to consider coherence and
>>explainability in the evaluation of research in mainline set theory.
>
>      Coherence is important, explainability much less so.

But I find that explainability is intimately tied up with coherence. And in
particular, the standards for a new mathematical method of reasoning to
become accepted is very very very high - in terms of coherence and
explainability. It's just not going to happen - unless it is for "normal"
mathematical purposes, is not regarded as a fluke, and is generally usable
and explainable and coherent.

>      One more point:  the question that we are to debate, "Does
>mathematics need new axioms?", is deficient. It leads into pointless
>wrangling as to what we mean by "mathematics" and "need".

I tend to agree with you to some extent. But we may be able to avoid a lot
of what you call "pointless wrangling" if we can agree in advance that if
the big conjectures that I am making turn out to be true, then, indeed,
mathematics needs new axioms - at least in the sense intended by the
organizers of the upcoming panel discussion. Exactly what those axioms
should say can be subject to debate.

>I would put the
>question a different way: Is the search for, and study of, new axioms
>worthwhile? It seems to me that this gets to the real, "applied
>philosophy of math" question: should people be working on this stuff?

I would say yes, definitely, but with an expanded approach that addresses a
range of fundamental issues that are not being properly addressed right
now. Also, there should be modifications in the associated educational
processes.