[FOM] Re: pom/fom. directions

[Harvey Friedman]

Reply to Corfield.

Notice that I changed the subject header. I hope you like it.

On 10/17/03 12:32 PM, "David Corfield"
<david.corfield at philosophy.oxford.ac.uk> wrote:

> I found myself in broad agreement with Harvey Friedman comments on
> Alasdair Urquhart's comments about my book.

>From reading Urquhart's comments, I didn't expect that. It's nice to hear.

>One thing I'd like to add
> is that it's not always the case that mathematics gets conceptually harder
> up at the frontiers of research. As you can see from the last chapter of my
> book, I'm indebted to the expository work of John Baez. One of his views,
> which he shared with the late Gian-Carlo Rota, is expressed in the
> following:
> 
> "...it makes sense to spend at least a little time going back and thinking
> about simple things. This can be a bit embarrassing, because we feel
> we are supposed to understand these things completely already. But in
> fact we do not. And if we never face up to this fact, we will miss out on
> opportunities to make mathematics as beautiful and easy to understand
> as it deserves to be." (Baez and Dolan, 'From Finite Sets to Feynman
> Diagrams', Mathematics Unlimited - 2001 and Beyond, also available
> online)

Judging by the way you put it, I would surmise that you think that
mathematics *usually* gets conceptually harder at the frontiers of research.

But I think we have not quite focused on a very important issue for any
philosopher (and other scholars outside professional mathematics) who wishes
to seriously look at mathematics along the scale from 1 through 10 that I
presented in my posting of 10/14/03 11:19PM, Comments on comments on
Corfield's book.

What is the value of modern mathematics from the philosophical or
foundational point of view? For that matter, what is the value of modern
mathematics, period?

There are two standard ways that people who know some modern mathematics try
to convince people that there is some value to modern mathematics.

1. It is beautiful.
2. It is deep.
3. It is extremely difficult.
4. It ties up with physics.
5. It is useful.

Obviously 2,3 are related, and 4,5 are related.

But note that none of these "reasons" has any prima facie connection with
what traditionally has been of concern for philosophers.

All of these five "reasons" have their serious strengths, but all of these
five "reasons" have their serious weaknesses.

I chose to focus on f.o.m. because by absorbing what happened particularly
in the 1930's, I saw only strengths. Strengths that I don't see either in
modern mathematics or in modern philosophy.

I won't go into these strengths and weaknesses at this juncture.

However, there is one clearly impressive achievement that perhaps some might
think that philosophers could achieve with regard to modern mathematics.

Can it be cast in such a way that not only is it more understandable to more
people, but actually assumes a compelling kind of obvious general
intellectual interest?

For this, things like 1-5 just won't do. I mean a way of casting it so that
it can arguably take an equal place alongside the great awe inspiring
intellectual achievements of all time?

In that famous TIME/LIFE 2000 book I discussed several times on the FOM,
among the list of 20 great thinkers of the 20th century, there were a few
physicists, 3 scholars concerned with f.o.m., etcetera, but not a single
core mathematician. The closest runner up in core mathematics was von
Neumann, again deeply concerned with f.o.m. (and many other things), and
again with a distinctly foundational attitude.

So one question is: can a philosopher prove that TIME/LIFE was misguided?

> One small example  from the field of combinatorics, where the concept
> known as a 'species' is beginning to take hold: one can understand
> much about the exponential function by knowing it corresponds to
> the species 'count set structures' on a finite collection. E.g., the fact
> the
> exponential function is unchanged under differentiation corresponds
> to the fact that the number of set structures on a finite collection (i.e,
> one)
> is not changed by tossing another object into the collection before
> counting set structures.
> 
> The complicated looking commutator relations for annihilation
> and creation operators turn out to reduce to the fact that
> there is one more way to toss an extra object into a collection
> then select one, than there is to select an object and then toss
> in an extra object.
> 
> Rota, whose advocacy of species was drawn to the attention of this
> list, describes the "bottom line" of his mathematical interests as the
> placing of balls in boxes. Continuing the species line, I had an
> exchange with Baez on sci.math.resesearch where it became clear
> that the appearance of the Bernoulli numbers in physics has much
> to do with the idea of putting things into boxes.

All this is nice and cute and even thought provoking. But it only hints at
something IMPORTANT at the level I am talking about above.

Of course, the same can be said of physics. Just because something appears
in physics doesn't mean that it has any special importance.

By the way, in case people didn't know: just because something appears in
philosophy doesn't mean that it has any special importance.

OK - just because something appears in f.o.m. doesn't mean that it has any
special importance.
 
> Still, the gap between philosophers and research mathematicians is extremely
> wide. As Friedman says,
> 
>> In the present culture, one can expect mathematicians to be about as good
>> at, or interested in, philosophy, as philosophers are good at, or
> interested
>> in, mathematics.
> 
>> From this a few comments:
> 
> Anyone making a serious effort to construct a bridge between the
> disciplines should be actively encouraged.

Yes, I agree, as indicated above. But I think that this is generally
worthwhile for philosophers ONLY IF they can realistically aim at making a
bridge between philosophy of obvious general intellectual interest, and
mathematics of obvious general intellectual interest.
> 
> Be especially generous to those putting down piles in the middle of the gap.
> (Martin Krieger's 'Doing Mathematics' might be taken as an example.)

I am sure that there are examples like that that at least start to go in a
good direction. 

A big problem in sorting out modern mathematics, and working with
mathematicians, is that mathematicians generally seem very eager to take
things in overly specialized directions, where the connection with the
original overarching intellectual goals are severed.

A big insight is made that becomes classical, with a clear relevance to
matters of obvious general intellectual interest. Technical ramifications
are pursued, without going back to the original grand motivation. Going back
to the original grand motivation is necessary in order to maintain the
obvious general intellectual interest. It is normally far more difficult to
come up with another blockbuster, and much easier to pursue the technical
ramifications. Sooner rather than later, the potentially grand subject just
becomes another ordinary subject with ordinary work by ordinary people doing
things of ordinary interest.

What is most frightening for many people is that upon going back to the
original motivation, one may see that in order to make the next grand
advance, one has to rethink the basic setup in order to take more phenomena
into account. This rethinking of the basic setup may render various
technical ramifications generated from the original grand advance completely
moot. Practitioners resist such rethinking of the basic setup in order to
preserve their status in the profession. They promulgate their "expertise"
in the irrelevant technicalities through their students and hiring policies.

This delays the next grand advances for decades, sometimes even longer. When
the next grand advances are made, they are resisted or met with mere
toleration. Finally, when the next grand advances gain enough force,
clarity, and visibility, they are fully accepted, as most of the
practitioners trapped in the technicalities of the original grand advance
have retired and/or become inactive.

Then the whole process repeats itself.

PHILOSOPHER'S BEWARE: if you venture into modern mathematics, you may come
into contact with people involved in grand advances operating with clear
motivating ideas of obvious general intellectual interest, or perhaps people
involved in technical elaborations on grand advances.

A question is: how can you tell who is who? Or can you get good at being
able to tell who is who?

> Let's learn as much as we can from parallel bridges, e.g. philosophy of
> science. An opportunity was lost in the reverse direction when
> philosophers ignored Polya's work. Whatever you think of the probabilistic
> approach to epistemology known as Bayesianism, much effort
> was expended by philosophers of science reinventing Polya's work.

Can you start an FOM thread regarding just what Polya did in this vein? The
general superficial impression among most people is that this was something
he wrote about connected with the fact that he lived to a ripe old age...

> We can be helped by the fact that as philosophers of physics continue to
> press forward to the physics of the past 30 years, they are learning
> plenty of frontier mathematics. We should combine to examine the
> role of mathematics in physics.

You know my view that we need to begin to understand physics that is
hundreds of years old from a foundational/philosophical point of view.

However, nobody seems to have really got this going properly yet, and so
perhaps your advice is OK - rather than getting nowhere with making
foundations of physics look like foundations of mathematics, and doing
general philosophy of science, one might as well do something like you
suggest...

I for one, will stick to trying to do something with ancient physics.
> 
> Many mathematicians are very generous with their time.
> 
> The greater the number of people engaged on the project, the less daunting
> it will seem.
> 
I take it that you are proposing Kreiger, and Baez/Dolan as a model?

In my posting Coments on comments... 10/14/03 11:19PM, I did make some
reasonably concrete suggestions connected with 1-10 there. I still believe
that concentrating on 5,6 there will be the most productive.

Harvey Friedman