FOM: new axioms panel
steel at math.berkeley.edu
Wed Feb 16 14:29:51 EST 2000
Some comments on Harvey's characterization (2/11/00) of my views:
> 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. I would add that the role of large cardinal
axioms in calibrating consistency strengths shows how central they are.
>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.
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. Newton must have known his theory of gravitation was such an
advance as soon as he had derived Kepler's Laws, if not before. I think we
know enough about large cardinal axioms and their consequences to see that
they represent a basic conceptual advance.
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. 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.
>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 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.
>In addition, my impression is that Steel feels that one cannot tell what
>mathematics will be important in the future, and thus it is unreasonable,
>unproductive, unfair, and irresponsible to criticize work in set theory
>on the grounds of lack of direct connection with matters of current
>interest to the mathematics community.
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. Second, I don't have any objection to informed
criticism in the proper forum.
>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?
>, 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.
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 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?
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