FOM: Significance and significant people
Neil Tennant
neilt at mercutio.cohums.ohio-state.edu
Wed Mar 18 12:58:36 EST 1998
In reply to Arnon Avron's and Torkel Franzen's comments in response to
my evaluation of the significance of Friedman's result, I need, I'm
afraid, to quote from what I wrote earlier, with some emphases added:
> [Friedman's] result *puts on an
> epistemological par* the two kinds of principle---combinatorial and
> large-cardinal. ... If I am told that
> someone has shown "A iff B", **when that sort of equivalence would have
> struck me, prima facie, as highly unlikely**, I don't question the
> significance of the proof of that equivalence by saying "Well, we'll
> have to wait and see whether A has any application; and we'll have to
> wait until we've settled the epistemological status of B." If A **looks
> like** the kind of claim that ought to be true **for simple reasons**, and B
> is the kind of claim of which I already know that many people claim
> not to know how one might come to know it, then I'm willing to state
> that I'm impressed.
It should have been clear that "ought to be true for simple reasons"
was elliptical for "ought, if true, to be true for simple reasons".
But I don't think that this ellipsis was the source of any of the
points that either Arnon or Torkel made in their rebuttals.
Arnon did not need to point out that a consistency statement is
already a combinatorial principle; and Torkel did not need to point
out that there is a difference between a large cardinal axiom and the
consistency statement concerning the same.
Torkel asked "if we have no ground for accepting [these combinatorial
principles] how do *they* advance our understanding of mathematics?"
(my emphasis added). The antecedent of the pronoun "they" is the
phrase "these combinatorial principles". But the question is not
whether the latter advance our understanding of mathematics. For the
claim of advance would have concerned the proof of their *equivalence*
with other, apparently much more problematic, principles. Torkel went
on to say "The epochal advance must be connected with *these specific*
combinatorial principles and *these specific* large cardinal axioms."
(My emphasis added.) Not so; the epochal advance intimated at this
stage is that for any proposed large cardinal axiom, Friedman's method
can be adjusted to provide a natural combinatorial principle that
turns out to be provably equivalent to the consistency of that large
cardinal. This would be an amazing domestication within the natural
numbers of the axiomatic clout of large cardinals assumptions in set
theory---a sort of Kroneckerization of any kappa you can imagine.
Imagine writing down, in primitive notation,
(B) Con(ZFC + existence of appropriate large cardinals)
so that its combinatorial character is explicit. Would the result
strike you as (i.e. look to you like) the kind of claim that ought,
if true, to be true for simple reasons? I think not, since you know
its provenance as, precisely, a consistency claim about an extremely
powerful extension of currently accepted mathematics.
It would be several orders of syntactic magnitude easier to write
down, in similarly primitive notation, Friedman's combinatorial
principle (A). Of this statement I would say that it looks to me like
the kind of claim that ought, if true, to be true for simple
reasons. Again, this is because I know its provenance as a claim about
inserting nodes in finite trees according to certain clearly stated
rules.
THEN one looks at Friedman's result, and learns that (A) implies
(B). One realizes further that, if one were ever to prove the
combinatorial principle (A), it could only be by dint of assuming the
existence of a large cardinal even larger than those whose consistency
is asserted by (B).
So much, then, for first appearances as to the imagined "simple"
v. "complex" reasons why a combinatorial statement is true (if it is
true).
To anyone who might raise the immediate objection that these prima
facie simplicity judgments cannot be formulated in a formal and
objective fashion, my reply would be that a similar complaint would
have to be true of *all* assessments of "significance", "importance",
"profundity", "elegance" etc. But that does not stop us from making
such assessments, and indeed letting those assessments guide us in our
choice of problems to work on.
Indeed, it would be a most interesting challenge to try to provide a
formal and objective theory of just what such significance,
profundity, elegance etc. *consist in*. Crudely put: would an adequate
theory of these intellectual classifications appeal more to the
mind-independent structure of the mathematical realm in question, or
to the psycho-biological-linguistic structures of the evolved
mind/brain?
What is it about any "deep theorem" or "elegant proof" or "powerful
method" or "fruitful definition" or "insightful lemma" or "enigmatic
conjecture" that appeals to the human intellect, reveals itself to the
human intellect, tantalizes the human intellect, etc.? Could there be
a metamathematical theory of this very phenomenon in mathematical
thought?
Assuming no progress on this kind of question for the foreseeable
future, we shall simply be left with judgments of interest,
significance, profundity etc. that are not wholly subjective---because
they are based on hard-won expertise in the area---but not wholly
objective either---because experts may not all agree.
Those who devote their lives to making great intellectual advances
have to take the risk that they will not earn the recognition they
deserve within their own lifetimes (e.g. Frege). Some will earn
recognition quite quickly among the relevant experts in the field, but
more widely only in their old age (e.g. G"odel), and may have to put
up early on with detractions, carpings, misunderstandings
etc. (e.g. Zermelo on G"odel). Yet others will achieve great eminence
by their prime, and enjoy enormous influence within the profession
(in terms of journal editorships, cohorts of students and assistants,
office-bearing in professional associations, influence on tenure
and promotions, etc.) but have their life's biggest projects fail, or
degenerate, or be attenuated by the contra-indicating results of
others (e.g. Hilbert).
And they all have personal defects of character. Frege was an
anti-semite. G"odel, when asked by an anxious Morgenstern about the
frightful conditions in Vienna, could answer only "Der Kaffee ist
erb"armlich"---and left behind him no fond anecdotes about his
greatness as a human being. Zermelo seems to have become a grumpy old
man. And Hilbert's arrogance was matched by his *anger* at G"odel's
2nd incompleteness theorem!
Did Hilbert publicly welcome and acknowledge G"odel's result as a
great breakthrough, deepening the collective quest for truth and
understanding? Hell no; he was simply put out by it.
One thing, at least, that could be said for G"odel (near mad man that
he was) was that he did not appear to need to be recognized for his
intellectual greatness, in order to find the inspiration to continue
with his work. The work appeared to be reward in itself. But he got to
hang out with the likes of Einstein and Morgenstern, no mean
conversational partners. His epochal work was over relatively
early in his prime; and he certainly did not produce really demanding
technical results (whatever their significance) after his 45th
birthday. (The 1958 Dialectica paper was written much earlier.)
Will we ever see someone achieve epochal results (by the standards now
set irrevocably higher by G"odel's legacy), who will overcome
carpings, detractions, misunderstandings etc., who will find the work
itself sufficient inspiration to continue, and who will produce their
best work (in terms of technical difficulty and intellectual
significance) at an age at which most others are well past their
prime?
It seems to me that, if anyone shows even a hint of promise at
fulfilling such specifications, the community would do well to nurture
his or her efforts by not imposing distractions in the form of
carpings, detractions, misunderstandings etc. For, history has surely
by now taught us enough about the near-impossibility of finding a
great foundationalist with the saintly virtues required to stand above
a fray over the significance of work that hardly anyone else is
equipped to do.
Neil Tennant
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