FOM: Classes/philosophical introspection/large cardinals
Harvey Friedman
friedman at math.ohio-state.edu
Tue Feb 15 11:49:28 EST 2000
Reply to Shoenfield Mon, 14 Feb 2000 23:14.
> In response to some rather unfavorable remarks I made about MK
>(Morse-Kelly set-class theory), Friedman has defended MK as natural
>and important.
It is, in my opinion, both natural and important. You can also make
isomorphic unfavorable remarks about Z_2 (the first order theory of second
order arithmetic). But I doubt that you would.
>Let me try to describe briefly what (in my opinion)
>is the origin and purpose of NBG and MK.
> For the moment, let us take a class to be a collection of sets
>definable from set parameters in the language of ZFC.
That is not a fundamental notion of class. It is a technical notion that is
not robust. For instance, you get more classes if you take collections of
sets that are definable from set parameters with quantification over not
only sets, but also the classes that you have just defined.
> Classes in
>this sense play an important role, even if one is working in ZFC.
Agreed. Classes in this technical restricted sense do play an important
role, even if one is working in ZFC.
> The nice thing about NBG it that every model M of ZFC has a least
>extension to a model of NBG; the classes in the extension are just
>the classes in M.
I would not say "classes in M". I would prefer the terminology "classes
definable over M." This is because the concept of class has an independent
meaning that is not properly reflected by just the classes that are set
theoretically definable.
>From this it follows that NBG is a conservative
>extension of ZFC. Thus whether we do set theory in ZFC or NBG is
>a matter of taste.
There are some interesting issues as to the length of proofs in NBG versus
ZFC. There is a known superexponential blowup in the conversion of a proof
in NBG of a sentence in set theory to a proof in ZFC of that same sentence
in set theory.
> Now all of this naturally suggests an extended notion of class,
>in which a class is an arbitrary collection of sets.
This concept of arbitrary collection of sets is not dependent on any of the
above discussion, and in fact, predates it.
>We then extend
>our class existence scheme to make every collection of sets
>definable in our extended language a class. Of course not every
>class (in the extended sense) is so definable; but these are the
>only ones we can assert are classes in our extended language.
In fact, this is why MK or MKC is so natural to consider. In fact, we can
make the following analogy:
PA, ACA_0, Z_2 (these are Peano Arithmetic, Arithmetic Comprehension with
set induction , and second order arithmetic)
and
ZF, NBG, MK.
The fundamental importance and role of Z_2 = second order arithemtic, i.e.,
the first order theory of second order arithmetic, has long been well
established. See, e.g., Simpson's book, Subsystems of Second Order
Arithmetic.
In exact analogy with the relationship between ZF and NBG discussed above,
we have, e.g., that every model of PA can be extended to a model of ACA_0
by taking as the sets of natural numbers, those sets of natural numbers
that are definable over the model of PA.
> Unfortunately, it is no longer true that any model of ZFC can
>be extended to a model of MK.
And it is no longer true that any model of PA can be extended to a model of
Z_2, as is well known.
>We can prove Con(ZFC) in MK by
>proving that the class V is a model of ZFC; and Con(ZFC) is a
>statement in the language of ZFC not provable in ZFC.
We can prove Con(PA) in Z_2 by proving that the class omega is a model of
PA; and Con(PA) is a statement in the language of PA not provable in PA.
>...In this way we can show
>(as Friedman observes) that a model V(k) where k is an inacessible
>cardinal can be extended to a model of MK.
In fact, there is a canonical, maximum such extension. Namely, V(k + 1).
>The trouble with such
>models is that they have strong absoluteness properties; most in-
>teresting set theoretic statements are true in V(k) iff they are
>true in V. This makes the models useless for most independence
>proofs.
The last sentence is true. However, the fundamental importance of MK and
MKC and other choicelike extensions is illustrated through the
consideration of these extremely natural and fundamental models - the
V(k+1) models. This is because MK and MKC and other choicelike extensions
comprise a more or less complete list of natural obvious axioms in the
language of class theory that hold of these very natural models.
Analogously, the fundamental importance of Z_2 and other choicelike
extensions is illustrated through the consideration of the extremely
natural and fundamental model consisting of the natural numbers and all
sets of natural numbers. This is because Z_2 and other choicelike
extensions comprise a more or less complete list of natural obvious axioms
in the language of second order arithmetic that hold of these very natural
models.
> Friedmann has given a sketch of an independence proof in MK by
>forcing; but many of the details are unclear to me. He takes a
>model M of MK, lets M' be the included model of ZFC and N' a generic
>extension of M'. He then says N' canonically generates a model N of
>MK. I do not understand how one selects the classes of N, nor how
>one can prove the axioms of MK hold in N. I would be surprised
>if the details wouls lead me to agree with Friedman that the question
>he was considering is "not very much easier to solve for NBG than it
>is for MK".
N' is obtained by adding a generic class over M'. I.e., the added class is
generic with respect to properties defined over M'. I meant to say that the
added class is generic with respect to properties defined in M. So we can
take the classes of N to be the subsets of N' that are definable over the
structure (M,N').
If we did the proof of the result for NGB + AxC instead of MK + AxC, we
could be taking N to be the subsets of N' that are definable over the
structure (M',N').
>In any case, there seems to be little reason to solve
>it for MK.
It is a sharper formulation of the result stated for a fundamentally
important theory of classes. The result answers a question that lies in the
context of work that precedes modern set theory - in fact, in Frege, where
notions of class are obviously relevant.
In such a context, it is completely wrong to prejudge the notion of class
to be that of extensions of set theoretically definable properties.
Shoenfield quotes me:
>> We have only the bare beginnings of where the axioms of large
>>cardinals come from or why they are canonincal or why they should
>>be accepted or why they are consistent.
> I agree whole-heartedly with this, and with the implied state-
>ment that these are important questions.
Shoenfield quotes me:
>> I have no doubt that further substantial progess on these
>>crucial issues will at least partly depend on deep philosophical
>>introspection, and I have no doubt concepts of both class and set
>>and their "interaction" will play a crucial role in the future.
> Here I strongly disagree. I think that if there is one thing
>we can learn from the development of mathematical logic in the last
>century, it is that all the major accomplishments of this subject
>consist of mathematical theorems, which, in the most interesing
>cases, have evident foundational consequences. I do not know of
>any major result in the field which was largely achieved by means
>of philosophical introspection, as I understand the term.
Many if not most of the most important developments in f.o.m. were obtained
by what I said: "at least partly using deep philosophical introspection" -
if not directly, at least indirectly in the formulation of decisive
theorems or in the choice of research programs. In fact, the most common
use of deep philosophical introspection in f.o.m. is the realization of
what the most significant issues and programs are. Of course, in most - but
not all - cases, a considerable amount of sheer mathematical power and
stamina is needed as well.
Examples:
1. Frege's invention of predicate calculus.
2. Cantor's development of set theory.
3. Russell's paradox and the theory of types.
4. Zermelo's axiomatization of set theory.
5. Turing's analysis of computation.
6. Tarski's formalization of truth.
7. Heyting's formal systems for intuitionistic/constructivist reasoning.
8. Gentzen's cut elimination and normalization.
9. Gentzen's consistency proof for Peano Arithmetic.
10. Godel's completeness theorem.
11. Godel's incompleteness theorems.
12. Godel's consistency proof of the axiom of choice and the continuum
hypothesis.
13. Godel's consistency proof of Peano Arithmetic by means of functionals
of finite type.
14. The invention and some of the development of computational complexity.
I hesitate to speak for Cohen. But when I talked to Cohen in the late
sixties at Stanford, he indicated that he invented generic sets partly
based on the idea of formalizing a concept of "randomness" or "random set
of integers."
In fact, I know of an exposition of forcing that I think is the clearest
and simplest, which starts from such a philosophically attractive
perspective. In fact, it is possible to make this essentially the only the
new idea, the rest being very standard set theoretic constructions which do
not inovolve forcing at all.
One should not forget the late William N. Reinhardt's work on large
cardinals - partly a result of deep philosophical introspection. This
proved quite influential.
The invention and some of the development of reverse mathematics - partly a
result of deep philosophical introspection.
And almost everything I have ever done in f.o.m. is partly the result of
philosophical introspection.
>I do
>not see the the study of the interaction of sets and classes has
>led to any very interesting results.
One can argue with this on face value, depending on how one interprets the
whole development of axiomatic set theory from Frege through Russell
through Zermelo and Frankel, out of the prior confusions that include the
pardoxes.
But my main point about this is that I am talking of the future. I suspect
that this interaction between sets and classes, and perhaps other related
notions such an intensional predication, hold the key to further
fundamental understanding of where these axioms for set theory and large
cardinals come from.
The fact that no one has seen their way through this philosophically rich
situation is just a reflection that this is the future - not the past or
present. We all agree that there can be new approaches to fundamental
matters.
A hint of this may be contained in the work I did a few years ago on
reaxiomatization of set theory by means of two universes. The axioms come
out strikingly simpler than usual, and also large cardinals come out in a
more unified and suggestive way than usual. I haven't discussed this in
much detail on the FOM yet.
Just thinking about sets in the usual way, as an isolated concept, does not
seem to lead to any fundamental understanding of what is behind the axioms
of set theory and of large cardinals.
> If the problems about large cardinals cannot be solved by philo-
>sophical introspection, how can they be solved?
I am saying that it has to be partly by deep philosophical introspection.
>Fortunately, I
>have available an example of how to proceed, furnished by the recent
>communication of John Steel.
I was very happy to see John Steel take the time to write for the FOM about
large cardinals.
>I think it says more about the prob-
>lems of large cardinals then all the previous fom communications
>combined.
I would like you to explain the meaning of this sweeping declaration.
Specifically,
i) what "problems of large cardinals" are you referring to in this sentence?
ii) what "previous FOM communications" lie within the scope of your comparison?
iii) are the following "problems of large cardinals"?
a) why should/should not large cardinals be accepted - or even noticed - by
mathematicians?
b) why are large cardinals are consistent?
c) why is/is not the hierarchy of large cardinals is canonical?
iv) how would you evaluate "previous FOM communications" in terms of their
bearing on a), b), c)?
>The idea is to examine all the results which have been
>proved about large cardinals and related concepts, and see if they
>give some hint of which large cardinals we should accept and what
>further results we might prove to further justify these axioms.
A better idea is to examine all the results which have been proved with
large cardinals, see why they have not yet had an effect on mathematics and
mathematicians, and see how large cardinals can be used to have an effect
on mathematics and mathematicians. This simply cannot be done by drawing
set theoretic, or descriptive set theoretic (higher than Borel)
consequences of large cardinal axioms. Also make a deep philosophical
analysis of set theory, starting at the most elemental level of
impredicative definitions, combining the set theoretic notions with other
notions as needed in order to uncover what is behind it all.
>We are still a long way from accomplishing the goal, but, as Steel
>shows, we have advanced a great deal since large carinals first
>appeared on the scene forty years ago.
Putting aside any recent breakthroughs on a) under current progress, we
have, in a sense, made very minimal real progress in 40 years.
We are still a long way from understanding a), b), c) above, and I do not
see how the mainline set theory research today is aimed at understanding
a), b), c) above - at least in any generally understandable terms.
We had already known by 1970 the influence of large cardinals on the lower
projective hierarchy. The expectation was that if we understand the
influence of necessarily higher large cardinals on the higher projective
hierarchy, then we would gain an understanding of the fundamental issues
surrounding large cardinals.
However, as far as I know - and I am quite prepared to be corrected - this
work with higher large cardinals and the higher projective hierarchy did
not shed any new light on the lower large cardinals and its influence on
the lower projective hierarchy. It just moved the context up to a point
where it is further away from mathematical practice.
Of course, I do not deny that extending the theory known around 1970 up
through the higher projective hierarchy is a natural and interesting and
worthwhile research project. But it does not seem to be getting at the
fundamental issues - at least in a generally understandable way. A
substantially different approach is needed to get at the fundamental issues
in a generally understandable way.
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