FOM: FOM is hot
Harvey Friedman
friedman at math.ohio-state.edu
Fri Aug 28 01:33:58 EDT 1998
I have been out of touch since 8/12/98, and since then there have been 70
(wow!) postings since then!! And on a wide variety of topics, and most of
them thoughtful and productive, interesting, and valuable!
Taking into account the professional level and number of the subscribers
and posters on the FOM, and the quantity, quality, and general interest of
the activity, is the FOM the most striking, useful, important, productive,
interesting, and/or successful professional academic e-mail list ever??
What are the competitors, and what can we learn from how they operate?
Regardless of the extent to which this is true, I am convinced that there
is a huge potential for improvement. For one, there is a huge untapped
source of passive subscribers who have a lot of interesting things to say.
Many of these people are among the most accomplished people in f.o.m. I'm
hoping that these important people see that the FOM is getting to be the
place of record for the real time interchange of ideas, opinions, and
sometimes results of f.o.m. interest. They can use the f.o.m. to record
their relevant ideas, opnions, and results, and get real time feedback
without having to rely on formal publication - which in most cases is not
practical (or at best very cumbersome) with regard to the issues discussed
here. In fact, I hereby threaten to expose the names of some of these
passive important people in the future!
Also, not everybody important and/or having valuable things to say is a
subscriber to the FOM. I think we should tell the relevant people that the
FOM is hot, and that it is a place of record. The activity is currently
archived, and discussion has taken place concerning the permanent existence
of the archive. Does anyone know about current or expected provisions for
the permanent storage of vital electronic documents?
Now I turn to trying to make the FOM better. I frequently see that the
discussion of genuine intellectual issues gets bogged down in arguments
about terminology. Then some people conclude that the argument is simply
over terminology, and thereby is a waste of time. Well, if the argument is
simply over terminology, then it is frequently a waste of time. However,
the argument over terminology usually obscures the real - and interesting -
disagreements and agreements.
My suggestion is that accomodations be made by modifying the terminology if
necessary so that the real discussion can begin. Sometimes, the real issue
can be joined by an imaginative associated question which is more
terminology free.
In my postings, I will explicitly attempt to diagnose and get past
terminological issues where appropriate.
Martin Davis wrote 11:01 AM 8.12.98:
>Harvey has suggested that recursion theorists would have been well advised
>to make the switch to asymptotic complexity theory. In general, I don't take
>kindly to suggestions that scholars would be better advised to work on
>something other than what interests them. In this particular case, I can't
>help noting that whereas recursion/computability theory BEGAN with a
>compelling proof of a separation principle (r.e. vs computable), asympotic
>complexity theory has mainly succeeded in posing (admittedly interesting and
>important) problems. If it turns out that P=NP (and who can be sure that it
>won't), much of the subject will collapse.
I was really talking about recursion theorists teaching, incorporating,
supporting, and working with complexity theory, not necessarily to the
exclusion of recursion theory. I also feel that this assessment of
asymptotic complexity theory leaves much to be desired. First of all, I
believe that the probability that P=NP is tiny, although I realize you do
not share this view. Secondly, there is #P and PSPACE, which are even more
unlikely to be the same as P. Thirdly, there are a host of other important
complexity classes, with some separations (e.g., logspace). Fourthly, does
anyone doubt that the solution to P=NP and a huge number of related
problems, regardless of which direction they go, will do anything other
than cause an explosion of rich, important, and extremely interesting work
in all sorts of directions? Just, for example, consider the impact on
crypotography. Granted, the subject may well evolve into something that
looks different than what it looks like now if the unthinkable happens -
that P=NP and related statements are true. But activity will be even more
feverish than it has ever been. It is also likely, in my opinion, that if
the unthinkable happens, that appropriate new complexity classes will
emerge which will be demonstrably different.
Mathias wrote 8:28AM 8/13/98:
>I remember Wolfgang Maass, who *has* shifted from recursion theory to
>complexity theory, telling me a few years ago that when he made that move
>he found his knowledge of recursion theory much less relevant than he
>had expected.
This reminds me of an important point about how fields of research are
often defended.
For any field X, people typically defend X by claiming that X is good for
something else that people more readily accept as important. Thus pure
mathematicians say that pure math is important for applied math. Applied
mathematicians say that applied math is important for science and
engineering. Scientists say that science is important for engineering.
Engineers say that engineering is important for industry. Industrialists
say that industry is important for the economy. Economists say that the
economy is important for the standard of living. Livers say that the
standard of living is important.
Of course, such statements vary greatly in strength. But most such
statements have an inherent weakness. That is, if you mainly defend X by
claiming that X is important for Y, and exploit the perceived importance of
Y, then the danger is that X will start to be judged largely in terms of
what it does and promises to do for Y. This is likely to create unrealistic
expectations for X, especially if the typical work in X is too remote from
Y.
The right way to judge research in fields is against an absolute standard
of intellectual interest. This includes as a special case, the importance
of a field in terms of its applications to another field, where the target
field has more intrinsic interest, independently of its applications to any
third field. E.g., it might well be that field A has little intrinsic
interest, but is very useful for field B, which on the other hand, has
great intrinsic interest.
Of course, the problem remains as to how to judge, or even explicate,
intellectual interest. I have previously called this "general intellectual
interest" (I also like "instrinsic interest") on the FOM. At this stage in
my career, I would rather try to systematically produce a large variety of
work of high general intellectual interest rather than spend too much
effort torward a theory of "general intellectual interest," for these
reasons:
1) such a theory, although badly needed, requires a great deal of work;
2) there is a shortage of people who produce work of high general
intellectual interest in a large variety of contexts in a systematic way;
3) there seems to be a chasm between people who understand and seek general
intellectual interest and people who don't; and it is an even much bigger
effort to develop 1) sufficiently so as to convert people who don't into
people who do;
4) i.e., with regard to 3), it is difficult to explain color to the color
blind, or melodies to the tone deaf.
Nevertheless, I have and will continue to make some general explanations of
general intellectual interest on the FOM.
So a question is: what is the general intellectual interest of recursion
theory? Well, some of it has considerable gii, and I emphasized open issues
of high gii in my 2:24AM 8/12/98 posting. I question the gii of much of its
current emphasis.
Martin Davis 10:35AM 8/13/98 wrote:
>I believe this happens regularly and expectedly in mathematics:
>
>1. A difficult longstanding problem succumbs to a new technique.
>2. The technique is quickly learned and applied to a bunch of problems.
>3. Harder problems require the technique be refined. Virtuosity develops.
>4. Virtuosos naturally go where their hard-won expertise is effective.
>Others may wonder whether it is all worthwhile.
>
>This is as natural as the tides. Telling talented people who have devoted
>enormous effort to becoming virtuosos that they should do something else is
>as pointless as telling a violinist to become a pianist.
>
>In a social setting where enough resources are found to permit talented
>people to do what they find interesting and worthwhile all of this is a
>non-issue.
However, we are not "in a social setting where enough resources are found
to permit talented
people to do what they find interesting and worthwhile."
There are really two practical problems. Firstly, I am sceptical that there
are enough such resources. Secondly, every field competes for the truly
talented in the sense of getting their attention and making the prospects
of spending their time there look attractive. QUESTION: How attractive does
recursion theory look in these terms? Mathematical logic? Pure mathematics?
Applied mathematics?
We are in an atmosphere where higher forms of intellectual acheivment are
not necessarily rewarded. In fact, most researchers are not even
consciously aware of these higher forms. Thus even the existence and
possibility of these higher forms is not exposed to the students.
There is an analogy in the musical world. There is a time tested concept of
technical virtuosity among violinists and pianists. However, the system -
fortunately - goes beyond technical virtuosity and into expressive musical
conception when it evaluates professional violinists and pianists at the
highest levels. The opinion makers consider this, and enough of the
audiences also consider this. Perhaps not as thoroughly as many would like.
But more than in math. In fact, I would say that no lasting professional
career in piano or violin performance can be had primarily through
technical virtuosity. E.g., Horowitz and Heifitz had much more.
If this were not true, then there would definitely be a gross downgrading
of musical culture. To some serious extent, we are in the midst of a gross
downgrading of mathematical - and intellectual - culture.
I would like to say that the FOM list is the magic cure. However, I will
resist saying that - now.
Martin Davis 4:14PM 8/13/98 wrote:
>1. I believe that much political discourse in the US over the past decade
>has been greatly distorted by the myth that resources (though finite of
>course) are much scarcer than they actually are. Of course, this is getting
>pretty far from F.O.M.
Well, in much of academia the resource problem is fairly easily documented,
and is in part caused by the fact that the U.S. acts as the employer of the
world. The last I heard, there are a significant number of mathematical
logicians looking hard for tenure track jobs; many without success. Suppose
talented person X comes into the job market, doing off the beaten track
work which is highly creative yet not spectacular. He/she has to compete
with all the others who are doing on the beatan track work which is not as
highly creative and also not spectacular. Good luck to X.
>2. If your Professor X is perceived to have real talent and the energy to
>employ it, then it will pay society in the long run to support his
>widget-classification. If even 1% of such do something that ultimately turns
>out to be really useful/important, it will have been an excellent
>investment. And past experience does not suggest that people have been very
>good at picking out the good bets ahead of time.
I claim to be "very
good at picking out the good bets ahead of time" but I don't get listened
to much, and people would rather follow the beaten track. Hence my
participation in the FOM list. I feel I can do better than
"widget-classification." I think the 1% figure is much too high, and I
would like to play a role in raising it up to 1%.
But how do we "pick out the good bets ahead of time"? By the kind of
critical and sometimes harsh analysis of what's going on and what could go
on. I.e., by the kind of interchange and challenges and criticisms that you
sometimes object to.
>3. As long as resources are seen to be not merely finite but so limited that
>supporting Prof. X means that some equally deserving Prof. Y will be left
>out, then political power, pull, friends in high places, cliques will
>inevitably (if regrettably) play a key role.
That's what's happening to some extent in the real world. Right now,
mathematical logic is being left out (to varying degrees) in math depts at
Princeton IAS, Princeton, Yale, Harvard, Cambridge UK, NYU, Columbia,
Austin, etcetera. And consider this: the GREAT ONE was at Princeton IAS,
and A. Robinson, MacIntyre were at Yale. What does this mean?
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