[FOM] Thoughts on CH 1

[Harvey Friedman]

Sol Feferman has put forward the thesis that

The Continuum Hypothesis is neither a definite mathematical problem nor a
definite logical problem

which is in fact the title of one of his recent preprints. I am one of many
scholars that Sol asked for comments.

I don't disagree with the general thrust of Sol's views here. However, I
feel more comfortable discussing CH in more practical terms.

I am not entirely comfortable with the notion "definite mathematical
problem" except in the context of contemporary and future mathematical
activity. I.e., I don't have a feel for the notion of "definite
mathematical problem" divorced from existing mathematical activity. In the
context of existing mathematical activity now, it is clear that CH is no
longer a "definite mathematical problem". An interesting question is: under
what circumstances would CH revert back to being a "definite mathematical
problem"? Sol does address this, and I have my own way of talking about
this below.

I see that there is perhaps a sense of "definite mathematical problem" that
is independent of the nature of actual mathematical activity. Sol relates
this to "inherent vagueness". I am indifferent to this phrase. Something is
inherently vague, to me, only until (or unless) someone manages to clarify
it. However, as a working foundationalist, I have to confront practical
forks in the road. See below.

I am also not entirely comfortable with the notion "definite logical
problem". I can be construed as working on "logical problems" but I don't
think of them that way. I view myself as working on "foundational
adventures", and this is not the place to try to discuss what these are.
Nevertheless I understand better the notion "definite problem in
mathematical logic", and by Sol's example of decidability of the field of
reals with exponentiation, he may well mean exactly what I mean. Again, an
interesting question is: under what circumstances would CH become a
"definite problem in mathematical logic"?  There do seem to be definite
problems in mathematical logic that have been raised and continue to be
raised in connection with CH research - even if they are not exactly CH..

I have clearer opinions about CH - actually the CH problem - iif we pass to
much more pragmatic terms.

I am a foundationalist, having concentrated heavily on f.o.m. (although I
want to further my intellectual development and broaden out).

>From the foundationalist perspective, the crucial pragmatic issue is this.
How promising is CH research in terms of expected results?

Actually, this is not quite the question the working foundationalist needs
to resolve. The real question for the working foundationalist is:

How promising is CH research in terms of expected results compared to other
f.o.m. research?

I had to confront more or less this question already before 1970, after my
work on Borel determinacy.

Soon after Cohen 1963, the enormous divide between the thrust of
mathematical research and research in set theory was already clear to
mathematicians and math logicians with logical/foundational sensibilities.
Checking with a few people who are quite a bit senior to me who were
observing the scene at the time, there was the burning question of whether
this independence from ZFC would enter "concrete mathematics". Sometimes
asked more specifically, "an arithmetic independence from ZFC".

I was in graduate school 1964-67, and I learned Godel/Cohen from Hillary
Putnam in Spring of AY 1964-65 - already then concrete or arithmetical
independence was known as a rather distant possibility.

I took a job in the Philosophy Department at Stanford in 1967, but my
office was in the math department. So I had easy access to talking to math
faculty at Stanford about logic, and of course Cohen was there full time.

What I remembered so vividly was the virtually total dismissal of any
distinctly set theoretic notion whatsoever as mathematically uninteresting
by just about all of the math faculty I talked to. Of course, they were
proud that one of their own had in their minds shown the "unsolvability" of
the most famous remaining set theoretic problem (CH), but they were
comforted by Cohen's virtual dismissal of math logic - as a branch of math.

After I proved in 1968 that Borel determinacy cannot be proved in Zermelo
set theory with AxC, in more technically, not provable any particular
V(alpha), alpha countable, I was at a crossroads about where to put maximum
effort. Borel measurability appeared to be a wonderful dividing line - not
too set theoretic, but not too concrete. I did venture a little higher up
in my fairly early career - I proved that analytic determinacy fails in all
set generic extensions of L (later sharpened by Harrington), and "there is
a PCA well ordering of the reals" iff "every real is constructible from
some fixed real", and used random real forcing in connection with Fubini's
theorem, and maybe some other odds and ends.

So by 1970 I saw a choice of getting involved higher up - with the
projective hierarchy and CH - or staying at Borel - or moving down to the
countable and the finite. There were four factors at play in my decision
not to move up.

Firstly, just looking at the math literature and prize awarded, it seemed
that even Borel is arguably much too much, let alone the projective
hierarchy. There seemed to be a natural flow of mathematical ideas
generated from geometrical intuition and counting, and the related set
theoretic ideas are very very tame and well controlled. At least for the
main thrust of what the mathematicians seem to really care about. They find
generality congenial if it SIMPLIFIES the mathematics. They don't like
generality at all if it COMPLICATES the mathematics by having to deal with
problem instances that they regard as irrelevant to the point of the
mathematics. When this arises, they will naturally gravitate to cutting
down the generality.

Secondly, the above was strongly reinforced by what appears to be the
painful visceral projection of disgust even at the mention of an overtly
set theoretic notion or context.

HOWEVER! - when a dose of set theoretic generality appears inside a proof
of something they are already interested in, then that is perfectly
acceptable. After all, mathematicians are frequently doing all sorts of
specialized things of no general interest inside proofs of deep theorems.
SUCH IS the case for FLT, and trying to prove this in finite set theory
(aka PA) is a daunting task - particularly if it is to be convincingly
documented. See work of Colin McLarty.

Thirdly, I saw impending doom for the foundations of mathematics if Goedel
Incompleteness were to stall without perfectly mathematically natural
concrete examples. Over time, I saw the prospect of Goedel Incompleteness
becoming rightly viewed as an amusing minor footnote in the history of
mathematics that is "known" to be inherently and profoundly irrelevant to
the ideas and purposes of mathematics.

Fourthly, from my discussions with many mathematicians already by 1970, it
was clear that the overwhelming majority of mathematicians implicitly
believed that new axioms for mathematics would be needed only for
"abnormal" questions, although they certainly did not have the tools or
even the vocabulary for articulating their implicit beliefs. Among the more
articulate mathematicians I met at Stanford regarding this issue was Halsey
Royden. It was clear already at the time - even going back to Godel/Cohen -
that analytic sets and PCA sets are not going to be handled decently in
ZFC. Of course I observed that the reaction among mathematicians was to
continue to stay away from analytic sets and PCA sets. Mathematicians find
it very easy to continue to stay away from them.

Fifthly, history has shown consistently and repeatedly that mathematical
areas thrive only if there is healthy and vibrant interaction with other
mathematical areas. If not, then the area will first be relegated to
research centers of less and less prestige, and finally have almost no one
earning a living based on research in the area. There is no question that
set theory is tempting that fate - clear now, and it started to look that
way by 1970.

So by 1970, I regarded the "perfect incompleteness" project as a much
better bet, overall, than CH research - given what was known by 1970. And
this is not the only foundational adventure I regarded as a better bet than
CH research. This is not the place to discuss them.

MAGIC BULLET FOR CH?

Having said this, I can assure you that if I was brilliant enough to have a
really promising idea about CH research, then I would certainly pursue it
vigorously. I do have some specific musings about it which I will wait to
discuss in "Thoughts on CH 2".

A magic bullet of course is that there is a missing axiom in ZFC, and when
this missing axiom is added to ZFC, we get a relatively consistent system
(or maybe relative to large cardinals) which decides CH. One which has the
compelling simplicity that all of the axioms of ZFC have, but which was
simply left out. E.g., Replacement was left out of Zermelo set theory. Also
at one point AxC was left out of ZFC, and although it can be argued that it
is quite different from the remaining axioms, it nevertheless has an at
least arguably compelling character, and is overwhelminingly simple
conceptually.

Of course, nobody believes that this magic bullet exists at least in this
strong form. I have raised the project of proving that this kind of magic
bullet does not exist.

A weaker magic bullet would be to relax the requirement that the axiom to
be added would be comparably simple to the existing axioms of ZFC.
Nevertheless, require that it be compelling in some substantial sense.
Perhaps   based on sophisticated forms of a major guiding principle of set
theory, namely, MAXIMIZE.

This is the so called "intrinsic" approach. As it is commonly understood,
it appears to have been abandoned by the set theory community except for Sy
Friedman (and collaborators), who I have known for over 60 years. It does
appear that this ambitious attempt at the "intrinsic" is fraught with
conceptual, philosophical, foundational, and technical difficulties, but Sy
is trying to surprise us with something at least partly compelling, even if
it is a long shot.

Instead, the bulk of the CH research is in the general category of the
"extrinsic". This is of course comparatively immune to the kind of
criticism that the "intrinsic" subjects itself to, since the "extrinsic"
can fall back on actual set theoretic practice and perhaps asthetic
considerations. So "extrinsic" is harder to criticize than the "intrinsic",
but on the other hand less spectacular and of less general intellectual
interest.

At this point, I am glad I threw my cards in with "perfect incompleteness
research" rather than "CH research".

CH A MATH PROBLEM?

As Sol says, this would happen if there was some preferred model or
preferred axiom system within which to evaluate truth or provability. Again
this splits into "extrinsic" and "intrinsic".

Of course, this already happened with L, which is intrinsic. Of course,
adhering to L is the arch opposite of MAXIMIZE. L represents a very robust
and coherent rejection of full set theoretic generality.

Set theorists have - as is well known - adapted the L idea to some large
cardinals. So called inner model theory program. I think it was started by
Jack Silver with L(mu). However, it has been stalled for decades, and some
experts are skeptical that it can be carried through for large large
cardinals. There is now a common idea put forth that "there is a compelling
case for the truth (weaker: the consistency) of a large cardinal hypothesis
if and only if there is an appropriate inner model theory for it". This
thesis does carry with it a number of associated theses about the very
nature of mathematics, including mathematical existence/truth, that beg for
elucidation and justification.

Incidentally, of course the "intrinsic" and the "extrinsic" could
conceivably merge into one, in set theory, but that seems way far off. In
the meantime, the distinction does seem to be clarifying and useful.

CH A PROBLEM IN MATH LOGIC?

It appears that the current CH research is too undeveloped for clearly
attractive open math logic problems asking for the status of CH in
particular models or theories to have emerged. My limited understanding is
that usually the status of the CH is easy in some model or theory, but the
hard problem is whether the model exists or has sought after properties, or
whether the theory is consistent (or consistent with other frameworks). But
I am be wrong here, as I haven't closely followed the details of CH
research.

In summary, as a foundationalist, my instinct is that CH research is not a
good bet for general intellectual interest or, generally speaking, the
spectacular. Of course, it turned out to be a good bet for Goedel and
Cohen. I chose to make other bets.

Harvey Friedman
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