[FOM] f.o.m. documentary 2

[Harvey Friedman]

Continuing the discussion surrounding my plans for the f.o.m.  
documentary

CAN EVERY MATHEMATICAL QUESTION BE ANSWERED?

THE DECLINE OF FOUNDATIONS OF MATHEMATICS.

The spectacular Golden Age of f.o.m. in the 1930s was followed by a  
period of more than 2 decades of much more specialized f.o.m.  
activity, where the results were no longer of general intellectual  
interest - with some arguable exceptions.

Incompleteness was the principal topic that drove the general  
intellectual interest in the 1930s, with associated issues surrounding  
the formation of and justification of the "rule book" for mathematics.  
This rule book, ZFC, is still in force today.

But Incompleteness became relatively dormant for about 25 years, until  
the unfinished work on incompleteness (from ZFC) and the continuum  
hypothesis left by Goedel was completed by Cohen in the early 1960s.

The Cohen development did bring f.o.m. back up to a substantial level  
of general intellectual interest - at least temporarily. However, the  
general intellectual interest steadily died down, for interesting  
reasons, which we now elucidate. These reasons are interesting and  
important, and we learn a lot by analyzing them - not ignoring them.

Mathematicians became aware of differences between the continuum  
hypothesis - and later examples of incompleteness from ZFC - versus  
what they work on and value in mathematics. Although generally not  
able to articulate the differences, it became apparent to the  
mathematicians that the differences were major and fundamental.

Soon after the Cohen development, Conventional Wisdom set in: that  
mathematicians have a natural protection from Incompleteness, in that  
simple, clear, transparent, well motivated, and concrete mathematical  
questions are difficult to answer only for substantive mathematical  
reasons - not because the ZFC rule book is inadequate.

For many decades, examples of simple, clear, transparent, well  
motivated, and concrete mathematical questions independent of ZFC were  
nowhere in sight, and the search for such was not regarded as a  
credible research program.

Unable to capitalize properly on its great successes in  
Incompleteness, f.o.m. lost its special status among mathematical  
subjects as being of singular general intellectual interest. This  
should not be taken too negatively. After all, very little is  
"singular".

Of course, good, very good, and better than very good, things were  
still being done in f.o.m. - just as good, very good, and better than  
very good, things were being done in most areas of mathematics.

THE EMERGENCE OF MATHEMATICAL LOGIC IN MATHEMATICS.

Meanwhile, in the 1960s, US mathematics departments were expanding  
rapidly, and the significant number of gifted mathematicians attracted  
by the Goedel and Cohen results - and other results outside set theory  
- were able to secure jobs in mathematics departments under the banner  
of "mathematical logic". The name "mathematical logic" is highly  
preferable to "foundations of mathematics" in the mathematics  
community, as the former sounds more mathematical, whereas the latter  
sounds more philosophical. Skepticism about philosophy within the  
mathematics community has long been, and continues to be, very high.

Soon after people schooled in f.o.m. migrated to mathematics  
departments, the scholars not only adopted the category "mathematical  
logic", but also abandoned f.o.m. issues as the motivator of their  
research programs.

The phrase "mathematical logic" has been around long before the 1960s,  
and a good working definition of mathematical logic, sensitive to  
current conditions, is: the mathematical spinoffs of f.o.m.

In the great events of f.o.m. up through the Golden Age in the 1930s,  
certain fundamental mathematical structures were identified and used.  
These fundamental mathematical structures formed the basis of what is  
now known as "mathematical logic". The information needed to be  
established about these fundamental mathematical structures for the  
primary f.o.m. purposes was rather limited.

Accordingly, it is quite natural to inquire much more deeply into the  
nature of these fundamental mathematical structures, far beyond the  
classic f.o.m. purposes.

So after the Golden Age of f.o.m. in the 1930s, mathematical logic  
developed in the mathematics departments generally independent of  
f.o.m. issues of general intellectual interest.

The mathematical logicians were housed in mathematics departments, and  
pursued detailed investigations of structures arising from f.o.m. -  
but not grand issues in f.o.m. itself. They presented themselves as  
working in a perfectly legitimate area of mathematics, like any other  
area of mathematics, with its own problems, its own concerns, and its  
own techniques. Since the mathematicians were not applying any  
standard of general intellectual interest to their own work,  
mathematical logicians did not feel that any standard of general  
intellectual interest should be applied to their work.

However, there was a vulnerability. The core mathematical areas very  
seriously interact with each other. They use theorems from each other,  
definitions from each other, and combined viewpoints. Mathematicians  
attach special interest to such interactions, especially when they are  
unexpected, and lead to yet more such interactions.

Mathematical logic had few such interactions, at least compared to  
interactions between other areas of mathematics. The status of  
mathematical logic within mathematics began to suffer accordingly,  
particularly as long term pressure on resources in pure mathematics  
set in (partly because of dwindling student demand, and partly because  
of the shift of resources to applied mathematics).

OPTIONS FOR MATHEMATICAL LOGIC.

Mathematical logicians saw four options in light of this situation.

1. Ignore this (the vulnerabilities created by lack of interaction  
with core areas of mathematics) and continue work as usual - detailed  
investigations of structures arising from grand issue f.o.m.
2. Focus on computer science issues, and join the computer science  
community.
3. Focus on developing interactions between mathematical logic and  
areas of core mathematics.
4. Focus on grand issue f.o.m. of general intellectual interest.

The majority of mathematical logicians chose 1, relying on the  
momentum generated by the original decisions from the 1960s to accept  
mathematical logic as a legitimate branch of mathematics.

A significant number of mathematical logicians chose 2, relying on the  
emergence of computer science departments, resulting in very rapid  
increased demand. This made sense for a number of mathematical  
logicians due to the common heritage surrounding Turing and  
theoretical computer science. A number of prominent mathematical  
logicians benefitted greatly from 2.

A significant number of mathematical logicians focused on extending  
interactions between mathematical logic and areas of core mathematics;  
i.e., 3.

An insignificant number of mathematical logicians focused on 4.

In focusing on deeper interactions between mathematical logic and  
areas of core mathematics, the mathematical logicians discovered some  
notions that are at least related to grand issue f.o.m. Perhaps most  
notable among these come under the general category of tameness.  
Tameness is a semiformal notion that refers to the well behavedness of  
certain fundamental structures. Mathematicians sense this well  
behavedness, but generally don't have the tools to state it in the  
most elegant and powerful way. Mathematical logicians often do, using  
one of the great structures emanating from f.o.m. - the first order  
predicate calculus with equality.

The mathematical logicians concerned with tameness issues generally  
focus on interactions with mathematics and not on grand issue f.o.m.  
Thus tameness is one of those notions important for f.o.m. that are  
not being further developed specifically for f.o.m.

REASONS FOR THE SHIFT FROM F.O.M. TO MATHEMATICAL LOGIC.

A combination of factors are behind the move away from grand issue  
f.o.m. to mathematical logic, and the focus on 3 above. Some of these  
factors are obvious.

Being housed in mathematics departments, there are compelling reasons  
to adopt many of the attitudes of mathematicians. The long term high  
level of skepticism among mathematicians of philosophy is one relevant  
attitude. Another relevant attitude is that mathematicians had long  
since abandoned any standard of general intellectual interest as a  
substantial component in the formation of research programs or in the  
evaluation of research. This much is obvious.

But the less obvious reason for the shift from f.o.m. to mathematical  
logic is that it is *extremely difficult* to make substantial progress  
on grand issue f.o.m.

The grand issues in f.o.m. often are not represented by previously  
stated purely mathematical questions. In fact, at this point in the  
development of f.o.m., grand issues in f.o.m. are not represented by  
previously stated purely mathematical questions - no exception comes  
to mind.

Even from the early days of f.o.m., the invention of the predicate  
calculus and the completeness theorem deal directly with grand issues,  
and didn't correspond to previously stated purely mathematical  
questions. The first and second incompleteness theorems did - perhaps  
even here there is an issue, historically, since the distinction  
between first and second order systems was so unclear at the time.

The work on the continuum hypothesis answered the grand issue "is  
there a mathematical problem, arising in the natural course of doing  
mathematics, or even a mathematical problem from the literature, that  
cannot be settled with the usual axioms and rules of mathematics?".  
This formulation of the grand issue of great general intellectual  
interest does not correspond to a previously stated purely  
mathematical question. However, depending on how fundamental one  
regards the continuum hypothesis itself, the work on the continuum  
hypothesis did answer a grand issue corresponding to a previously  
stated purely mathematical question - can the continuum hypothesis be  
settled within ZFC? But obviously, this formulation is of considerably  
less general intellectual interest than the previous formulation.

More recently, the principal embodiments of tameness (e.g., o- 
minimality) aren't answers to previously stated purely mathematical  
questions. The invention of Reverse Mathematics (and Strict Reverse  
Mathematics) aren't answers to previously stated purely mathematical  
questions.

So the enormous challenge in grand issue f.o.m. today is to

i. recognize what the grand issues are, or should be.
ii. recognize which ones are of the highest general intellectual  
interest.
iii. create appropriate formal structures that directly bear on the  
grand issues.
iv. create appropriate purely mathematical questions associated with  
the grand issues.
v. identify standards for evaluating success in attacking grand issues.

There is essentially no training in Universities for work of this  
kind, and little recognition that this is even a legitimate mode of  
mathematical research.

This kind of research, long since largely alien to mathematics, is now  
largely alien to mathematical logic.

IDEOLOGY AWAY FROM F.O.M.

Recall these options

1. Ignore this (the vulnerabilities created by lack of interaction  
with core areas of mathematics) and continue work as usual - detailed  
investigations of structures arising from grand issue f.o.m.
2. Focus on computer science issues, and join the computer science  
community.
3. Focus on developing interactions between mathematical logic and  
areas of core mathematics.
4. Focus on grand issue f.o.m. of general intellectual interest.

As some successes with 3 built up, a certain ideology took hold,  
popular among many, to varying degrees, of those involved in 3.

The ideology states that the point of mathematical logic is to provide  
tools for core areas of mathematics.

There are various embellishments of this ideology, which also have  
considerable adherents. For example,

a. Research in mathematical logic should be evaluated in terms of its  
relevance to core mathematics.
b. Research in mathematical logic should be evaluated in terms of its  
usefulness to core mathematicians.

Whenever I have heard these views, it has always been accompanied by a  
rather uncritical acceptance of the intrinsic importance of  
mathematics independently of its relevance or usefulness to anything  
else.

One also encounters views of those engaged in 3, of this kind:

c. Foundations of mathematics is an outdated research paradigm that  
has no relevance to modern mathematics, and outdated relevance even to  
modern mathematical logic.
d. Foundations of mathematics never had a special place in the history  
of mathematics, and its historical impact on mathematics is greatly  
overblown.
e. Foundations of mathematics never had a special place in the history  
of mathematical thought, and its historical impact on mathematical  
thought is greatly overblown.
f. Foundations of mathematics never had a special place in the history  
of ideas, and its historical impact is greatly overblown.

I don't have space to address the various issues raised by such views  
a-f in this posting.

But I want now to emphasize that a major ingredient in the emergence  
of such views has been the extreme difficulty involved in making major  
progress on grand issue f.o.m.

Thus, in addition to practical considerations connected with being  
housed in mathematics departments addressed above, mathematical  
logicians didn't generally see the option of emphasizing grand issue  
f.o.m. as viable.

In fact, given the great difficulties in dealing with grand issue  
f.o.m., using grand issue f.o.m. as the major research paradigm was  
viewed by many as risky. The danger is that it becomes difficult to  
promote the importance of what people are actually achieving.

Consequently, mathematical logicians developed peer groups, without  
connections to grand issue f.o.m. Each of the four main peer groups  
have its roots in grand issue f.o.m. They are, alphabetically, model  
theory, proof theory, recursion theory, and set theory.

Model theory from Frege's predicate calculus, Goedel's completeness  
theorem, and Tarski's axiomatization of real closed fields and geometry.

Proof theory from Hilbert's program, Goedel's incompleteness theorems,  
and Gentzen's completeness and consistency theorems.

Recursion theory from Church's Thesis, Turing's model of computation,  
and its extension to oracle computation.

Set theory from ZFC, and the Goedel/Cohen work on the continuum  
hypothesis.

NEW GOLDEN AGE OF F.O.M.?

Despite relatively quiet period for grand issue f.o.m. lasting several  
decades, I now believe that we are entering a new Golden Age for  
f.o.m. However, the full realization of this will require

i. a general realization that it is now feasible to seriously address  
grand issue f.o.m. yet again - not just in the 1930s and briefly in  
the 1960s.
ii. a general understanding of the great advantages in working much  
closer to grand issues of general intellectual interest than has  
become the norm in mathematical logic - or more widely, in mathematics.
iii. a general rejection of the ideology seeking to marginalize f.o.m.  
as discussed above.

Here are some developments, which I have been involved with, to  
varying degrees, that suggest a Golden Age. Many of them have  
developed gradually. I think that all of them have reached a critical  
level where great optimism is warranted.

1. Concrete Mathematical Incompleteness. After the Godel/Cohen work on  
the independence of the continuum hypothesis from ZFC, the grand issue  
was the extent of Incompleteness. It soon became clear that  
Incompleteness pervaded virtually all of set theoretic mathematics.  
However set theoretic mathematics had been largely marginalized as of  
a wholly different character than core mathematical interests. After  
many decades, Concrete Mathematical Incompleteness has now reached a  
sufficiently ripe stage of development.

2. Reverse Mathematics. The mapping out of the logical structure of  
mathematics from the RM point of view is well under way, and will  
become yet more systematic and thorough. Here, the obvious grand issue  
not addressed by RM is whether the theory can be reworked without a  
base theory, in some appropriate sense. I.e, so that the logical  
strength comes solely out of the mathematics itself. This leads to

2. Strict Reverse Mathematics. This is Reverse Mathematics without a  
base theory. My initial paper on this is in LC06.

3. Set theory as an extrapolation of finite set theory. I have  
lectured on this, and posted on this on the FOM.

4. Concept Calculus. I have lectured on this, and there are papers on  
my website. My initial paper on this is has appeared in Infinity, New  
Research Frontiers, Cambridge U. Press.

5. Tameness of mathematical structures. The most familiar well  
developed part of this is o-minimality. But the subject is far  
broader, and it will become more systematic and thorough. Also, when  
structures appear to be wild in various standard senses, it will be  
seen how they are still tame in various important ways.

These and other topics have a good chance of leading to grand issue  
f.o.m. developments of clear general intellectual interest.

The f.o.m. documentary project CAN EVERY MATHEMATICAL QUESTION BE  
ANSWERED? starts with that grand issue of general intellectual  
interest, and flows naturally into, at least, 1-5.

The intention is that the documentary series become the place of  
record for a clear and creative presentation of state of the art  
f.o.m. for at least professional - and aspiring professional -  
intellectuals. How deeply it penetrates into the general literate (and  
illiterate!) culture remains to be seen. The science videos I think  
have penetrated to a reasonable extent into (at least) the general  
literate culture. I have the same hopes for this f.o.m. documentary  
series.

Harvey Friedman