[FOM] f.o.m. documentary 2
Adam Lesnikowski
adam at math.berkeley.edu
Fri Feb 17 02:12:22 EST 2012
Great idea for a f.o.m. documentary, I would be excited to see it once it's
finished!
Regarding f.o.m.-related general audience documentaries and to get a sense
of what's been done, I would recommend these two recent ones from the bbc.
The first's on infinity, and the second's on cantor/boltzmann/turing/godel:
"To infinity and beyond": http://www.youtube.com/watch?v=KNJgXbAFmmQ
"Dangerous knowledge":
http://www.youtube.com/watch?v=vVWbWSkh6lI&feature=results_main&playnext=1&list=PL9D37605FD02395F0
Best wishes,
Adam
On Sun, Feb 12, 2012 at 8:49 PM, Harvey Friedman <
friedman at math.ohio-state.edu> wrote:
> 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
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