Is the theory of topological vector spaces still alive?
s.s.a...@gmail.com
A few years ago I wrote a paper where the theory of topological vector
spaces was called a dead science:
S.S.Akbarov. Pontryagin duality in the theory of topological vector
spaces and in topological algebra. Journal of Mathematical Sciences.
113(2): 179--349 (2003).
After its publication I received two protests from two mathematicians
who specialized in this science. That was a big surprise for me, since
for a long time my criticism at this address did not meet any
protests.
Unfortunately in both cases the discussion stopped at the stage of
specification of claims. However this question -- whether the theory
of topological vector spaces is dead or alive? -- intrigues me very
much. Perhaps, the picture from Russia looks somewhat more sorrowful
than it really is, so I am curious now if there are any people abroad
who could argue with me?
My point is that the main results in this theory were formulated in
1960s, and now people either apply them to other disciplines, or,
those few who remain faithful, study things useless for remaining
mathematics.
I am writing now another paper where I plan to mention this question
casually, so I will be grateful to everybody who could discuss this
with me.
Thank you in advance,
Sergei Akbarov
tc...@lsa.umich.edu
<s.s.a...@gmail.com> wrote:
>My point is that the main results in this theory were formulated in
>1960s, and now people either apply them to other disciplines, or,
>those few who remain faithful, study things useless for remaining
>mathematics.
This is a topic where the risk of debaters "talking past each other" is
great. To reduce this risk it may help to be more precise at the outset.
Definition. Let T be some interval of time. A mathematical field F is
"alive during T" if, during T, some new theorem in the field F is proved
and applied to some other field F'. A mathematical field is "dead during T"
if it is not alive during T.
Then it seems that you are making the following conjecture.
Conjecture 1. The study of topological vector spaces was dead during the
period 1970 to the present.
Additionally, your choice of the word "dead" (as opposed to, say, "dormant")
suggests that you may also be conjecturing the following.
Conjecture 2. The study of topological vector spaces will continue to be
dead for all time in the future.
Do these conjectures capture your question reasonably well?
--
Tim Chow tchow-at-alum-dot-mit-dot-edu
The range of our projectiles---even ... the artillery---however great, will
never exceed four of those miles of which as many thousand separate us from
the center of the earth. ---Galileo, Dialogues Concerning Two New Sciences
s.s.a...@gmail.com
Tim, it is clear for me that if we take your definitions, then we
never come to conclusion that any field of science is dead. The very
first your conjecture --
Conjecture 1. The study of topological vector spaces was dead during
the period 1970 to the present.
-- is formally not true, since there were some results in this science
after 1970, for example the famous Enflo and Szankowski
counterexamples (1973 and 1981 respectively).
As to the second one,
Conjecture 2. The study of topological vector spaces will continue to
be dead for all time in the future.
-- it is so severe that becomes useless, since we cannot be sure that
anything, or even anyone, will be dead for all time in future.
Even when a person dies we cannot be sure that this will last forever,
since in future the human can contrive something like time machine,
and this person will be alive again. (To say nothing about people’s
religious belief that the death lasts only to the Last Judgement.)
When writing that the theory of topological vector spaces is dead I
had in mind that the current investigations in this science seem to
be useless for the other parts of mathematics. There are many examples
of such situations, for instance Set Theory. Every mathematician now
uses the results of Set Theory. But can we say that Set Theory is
alive? People, who conceptualized this filed of mathematics, have
built some useful construction named now Set Theory, and we can say
that this work is finished by now, since for a long time there were no
useful improvements in this area. At least I did not heard about them
(of course, if you are a specialist in Logic, you can correct me).
And a similar situation is in the theory of topological vector spaces,
but the difference is that, first, the circle of mathematicians who
use their results is much more narrow, and, second, the circle of
those who claim that they “continue investigations in TVS” is a little
bit wider.
So I have been meaning to ask people, in which situations one can say
that this or that theory is dead? The specialists in the theory of
topological vector spaces seem to feel hurt, when I try to speak with
them about the “philosophy” of their science, but how do they expect
people to discuss such questions? -- This is a puzzle for me.
tc...@lsa.umich.edu
<s.s.a...@gmail.com> wrote:
>Conjecture 1. The study of topological vector spaces was dead during
>the period 1970 to the present.
>-- is formally not true, since there were some results in this science
>after 1970, for example the famous Enflo and Szankowski
>counterexamples (1973 and 1981 respectively).
I think you may have missed a crucial part of my definition of "dead," which
is that to be alive, some new theorem during the time period *must be applied
to some other field*. Doesn't that capture your notion of "uselessness"?
>Conjecture 2. The study of topological vector spaces will continue to
>be dead for all time in the future.
>
>-- it is so severe that becomes useless, since we cannot be sure that
>anything, or even anyone, will be dead for all time in future.
I agree with you, but I stated this conjecture partly to indicate why people
might feel "hurt" when you call a field "dead." If you call a field "dead"
rather than "dormant," then people may (incorrectly, but understandably)
infer that you implicitly believe Conjecture 2.
>Every mathematician now uses the results of Set Theory. But can we say
>that Set Theory is alive?
A good candidate for this would be Harvey Friedman's results showing that
large cardinal axioms are needed (in a very strong sense) to prove certain
concrete combinatorial statements that are fairly natural-looking.
Depending on what you count as set theory, one also has Soare's application
of recursion theory to differential geometry, or Hrushovski's application
of logic to algebraic geometry.
s.s.a...@gmail.com
> is that to be alive, some new theorem during the time period *must be applied
> to some other field*. Doesn't that capture your notion of "uselessness"?
Excuse me. Yes, I would agree with this. But as far as I can see,
usually such explanations are too vague to be convincing. When I ask
people, why their science is useful, they usually say me something
like: “people study this class of spaces, so this is the evidence that
our science is important”. Sometimes they add that some their results
allow to prove something “very important” in other sciences, but
immediately it turns out that these “applications” sound even more
ugly than the results that allow to prove them, and their “importance”
is at minimum grossly exaggerated. The chain always ends up on the
second link, and you suffer disappointments. In my opinion, this is a
serious problem in modern mathematics.
But maybe I ask wrong people. Your examples sound more reasonable:
> >Every mathematician now uses the results of Set Theory. But can we say
> >that Set Theory is alive?
> A good candidate for this would be Harvey Friedman's results showing that
> large cardinal axioms are needed (in a very strong sense) to prove certain
> concrete combinatorial statements that are fairly natural-looking.
> Depending on what you count as set theory, one also has Soare's application
> of recursion theory to differential geometry, or Hrushovski's application
> of logic to algebraic geometry.
Could you give me references? And do you know such examples in
topological vector spaces?
tc...@lsa.umich.edu
As I understand you now, the "problem" in question is the proliferation of
research articles on hyper-specialized topics that are of no interest to
anyone besides the hyper-specialists. Though I agree that such situations
exist and that the papers in question are of limited interest, I would like
to make two points:
1. I don't believe that the situation is worse today than it used to be, and
I don't think that mathematics suffers from the problem more than in other
fields. Pick a random scholar in a random academic subject from a random
period in history, and that scholar will assure you that the problem is
particularly bad in that subject and at that period in time.
2. It's not clear to me that it's a "serious problem." Rather, it seems
to me to be mostly harmless, a modest price to pay for the numerous good
papers that get written. Moreover, I've suggested more than once already
that "dormant" may be a better word than "dead." Sometimes a field of
mathematics undergoes a period of internal development which most outsiders
think is an example of the aforementioned undesirable hyper-specialization,
but then emerges as a powerful and unexpected tool later on.
>Could you give me references? And do you know such examples in
>topological vector spaces?
I don't know examples in topological vector spaces, but that's because I
know very little about topological vector spaces.
For the application of computability theory to differential geometry, see
Robert Soare's article "Computability theory and differential geometry"
which you can easily find on his website. Computability theory, or
recursion theory, was dormant for a long time in the sense that there were
few if any spectacular applications to other areas of mathematics, and
outsiders might have felt that the specialists were just diddling around
constructing ever-more arcane and intricate priority arguments to prove
uninteresting theorems. However, now we have examples of deep insights
into differential geometry whose only known proofs use sophisticated results
from computability theory.
For Harvey Friedman's results, you can again look through the downloadable
manuscripts on his homepage, particularly those mentioning large cardinals.
Large cardinals have been intensively studied by set theorists, but most
mathematicians regard them as totally irrelevant to the rest of mathematics
(if they even know what large cardinals are). However, Friedman has argued
strongly that in the not-too-distant future we will find large cardinal
axioms intruding in many different areas of mathematics, simply because
there's no other way to prove certain highly desirable theorems. In his
soon-to-appear book "Boolean Relation Theory," he gives families of
innocuous-looking statements, all of which are minor variations of each
other (obtained by replacing union with intersection, or a set with its
complement, etc., in the statement of the theorem), with the remarkable
property that all but one of the statements have nearly trivial proofs,
but where the one exception requires a large cardinal axiom (i.e., an
axiom going beyond the usual ZFC axioms of set theory) to prove. The
point is that large cardinals, despite their seemingly arcane definitions,
contain some very natural combinatorial, set-theoretic structure that
could potentially show up in nearly any branch of mathematics. For another
example, see the last section of Martin Davis's article "The Incompleteness
Theorem" in the April 2006 of the Notices of the AMS.
In both these cases, I believe that what rescued the subjects from total
irrelevance and oblivion was the excellent taste of the best practitioners,
who managed to identify the natural questions and the natural structure
intrinsic to the mathematical objects being studied, and who pursued this
natural structure relentlessly. The result was "unreasonable effectiveness"
to other areas of mathematics.
As mathematicians we are used to balancing the need to stay connected to
applications to science and engineering with the need to pursue pure
mathematics without immediate regard for applications. The same balancing
act is important *within* mathematics. Yes, we should guard against
hyper-specialization, but we should also make allowances for periods of
"dormancy."
An interesting recent case in point that was debated in the Letters
section of the Notices of the AMS was Friedrich Wehrung's solution to
Dilworth's longstanding Congruence Lattice Problem. According to a letter
in the June 2007 issue of the Notices, Wehrung's brilliant paper was
rejected by the Journal of the AMS for "lack of interaction with other
areas of mathematics." The letter criticized this decision severely.
The editors of JAMS responded that they receive more first-rate papers
than they can accept, and that a rejection does not mean that the paper
is bad. This is surely true. However, the editors did not comment on the
issue of "lack of interaction with other areas of mathematics." If this
alleged lack of interaction was indeed the primary reason for rejecting
Wehrung's paper, then in my opinion the editors of JAMS made a mistake.
A random paper in lattice theory with no connection to other areas of
mathematics is one thing; a brilliant solution to the Congruence Lattice
Problem is quite another. Outstanding mathematics can be recognized as
such even if there is no immediate application outside the subfield; we
should not need to wait for the next "unreasonably effective" application
of lattice theory to recognize the importance of Wehrung's work.
Stephen Montgomery-Smith
> Dear colleagues,
>
> A few years ago I wrote a paper where the theory of topological vector
> spaces was called a dead science:
>
> S.S.Akbarov. Pontryagin duality in the theory of topological vector
> spaces and in topological algebra. Journal of Mathematical Sciences.
> 113(2): 179--349 (2003).
>
> After its publication I received two protests from two mathematicians
> who specialized in this science. That was a big surprise for me, since
> for a long time my criticism at this address did not meet any
> protests.
Let me jump into this discussion. I really don't know much about the
culture of topological spaces, but I am rather well acquainted with the
culture of Banach spaces. I talk in terms of "culture" rather than the
"theory" because it is the aspects of how these theories relate to our
current culture that you are really talking about. I feel no qualms
about restricting to Banach spaces, because the examples you raised
earlier (the Enflo and Szankowski counterexamples) were really a part of
the Banach space culture.
In the same vein as these examples is the rather more recent
counterexample of Gowers and Maurey. That people work actively on this
kind of stuff is evidence, perhaps, that the area isn't dead.
But what disturbs me most about this kind of stuff is that it is full of
counterexamples. In the study of infinite dimensional Banach spaces, it
seems that almost all plausible conjectures have some very horrible
counterexamples.
Furthermore, the Banach spaces (or even TVS) that are used in real
applications (Sobolev spaces, Schwartz spaces) are trivial when
considered within the abstract theory of Banach spaces, so that the
counterexamples of Enflo and Gowers and Maurey are utterly divorced from
the reality that most people work with.
Contrast this, with say, harmonic analysis. There, all the decent
conjectures turn out to be true (e.g. Fefferman's BMO duality result).
Furthermore this stuff turns out to be utterly relevant to such things
as how differential equations work.
Or to put it another way, TVS simply doesn't fit into Eugene Wigner's
essay "The Unreasonable Effectiveness of Mathematics in the Natural
Sciences."
I don't know whether you want to describe TVS as dead, but it is
definitely not healthy.
Stephen
Keith A. Lewis
I'm not a practicing mathematician these days, but recall with
fondness reading Robertson and Robertson _Topological Vector Spaces_
as a grad student, so set your prior.
As an fledgling assistant professor, I worked on the invariant
subspace problem for bounded linear operators on a Hilbert space.
My current hobby is Category Theory, in case you want to update
you prior.
In general, the fewer axioms a theory has, the more difficult it
is to classify. Finite simple groups were classified long after
Killing did the equivalent for Lie groups. (Elie Cartan fixed that
up.) I heard Mary Ellen Rudin give a talk where she said she refused
to consider a topology unless it was at least T_1.
There are even better examples of Enflo's counterexample. I've
forgotten who proved this, but there are bounded linear operators
on a nuclear Frechet space that have no nontrivial invariant
subspaces.
Beurling's Theorem is a great example of getting to the bottom of
things. I can't imagine what more there is to say about the invariant
subspaces of the unilateral shift operator, but maybe someone else
will come along and point out what the rest of us missed. Fefferman's
BMO result turned out to have a much simpler proof using probability
theory.
One mystery to me is why vector spaces are so simple to define,
yet can be classified by dimension. Mac Lane and Eilenberg used
the double dual of linear operator as an example of a natural
transformation in their first paper on category theory.
--
s.s.a...@gmail.com
new one, because I again found mistakes there. Excuse me my English,
and thank you in advance, Sergei Akbarov.
------------------------------------------------------------
Tim, I do not agree with you.
> 1. ...Pick a random scholar in a random academic subject from a random
> period
> in history, and that scholar will assure you that the problem is
> particularly
> bad in that subject and at that period in time.
Of course, what we discuss here happens very often in different parts
of mathematics. But this does not mean that everywhere the situation
is the same. For instance, Stephen mentioned here Banach spaces.
Although, I am not impressed by what happens in the theory of Banach
spaces, I nevertheless presume to prove that situation there is better
than in topological vector spaces.
My proof is as follows. From the point of view of category theory the
difference between Banach and non-Banach situations is that in the
first case the theory suggests a convenient class of objects that form
a monoidal closed category (namely, class of Banach spaces) and for
each monoid in this category (here monoids are nothing more nor less
than Banach algebras) the corresponding modules over this monoid form
enriched category over the initial category (of Banach spaces).
In the theory of topological vector spaces the situation is absolutely
different. For its lifetime this science did not create any class of
spaces, convenient from the point of view of the customary algebraic
intuition, i.e., a class that, like the class of Banach spaces, one
could put into the place of the usual vector spaces in pure algebra.
For those readers who are far from the category theory, this idea
becomes clear after consideration the construction of algebra of
endomorphisms. As is known, in pure algebra every module $X$ over an
algebra $A$ generates an algebra $End_A(X)$ of endomorphisms of $X$
over $A$. This elementary fact ceases to be true in topological
algebra, if we require algebras and modules to be complete (in some
sense, general for all algebras and modules), and to have continuous
multiplication (again in some sense, general for all these bjects).
This can be conveniently illustrated by the following
Exercise. Give a definition of topological algebra and topological
module such that the following conditions hold:
1) all the topological modules are topological vector spaces and
satisfy some standard condition of completeness (we need this to
provide the convergence of natural nets and series);
2) the multiplication operations are continuous in some reasonable
sense;
3) there is a natural procedure that endows the ring $End_A (X)$ of
all endomorphisms of a given topological module $X$ over a given
topological algebra $A$ with the structure of topological algebra with
respect to your definition.
You may be surprised, but up to the last time the only known solution
of this Exercise in the frame of the theory of TVS was the class of
Banach algebras and modules. (Note by the way that the appearance of
Banach spaces is not a merit of the theory of TVS, since historically
Banach spaces were studied before the general topological vector
spaces. Moreover it was the narrowness of the
class of Banach spaces that has lead to the appearance of the theory
of TVS.)
On hearing this one may ask: "What were you, specialists in
topological vector spaces, doing all this time?" I asked them similar
questions, and if we translate what they usually answer to the normal
langauge, the translation will be as follows: "Our counterexamples are
more interesting for us. This is what we are proud of!"
So my first counter-argument is that the situation in different parts
of mathematics is not the same, and we can compare it (here I agree
with Stephen). And in this comparison the situation in the theory of
TVS looks scandalous.
> 2. It's not clear to me that it's a "serious problem." Rather, it seems
> to
> me to be mostly harmless, a modest price to pay for the numerous good
> papers
> that get written. Moreover, I've suggested more than once already that
> "dormant" may be a better word than "dead."
I do not agree with this as well. This is not very important, but,
first, I want to say that I do not see "numerous good papers that get
written" in the theory of TVS. And, second, I had not opportunity to
make an experiment, but I am sure, if I replaced "dead" with "dormant"
in my paper, the reaction would be the same: irritation.
My main counter-argument here is as follows. If the idea that the
hyper-specialization is a modest price for the progress becomes
dominant in scientific society, and people imply from this that we
should not be too exacting to what those "hyper-specialists" do, then
we inevitably come to a situation when those "hyper-specialists" abuse
their power.
In practice this abuse looks as follows. When you are a student they
tell you that this or that mathematical result "is very important and
elegant", and despite your doubts, you have to spend your time on
studying innumerable counterexamples (which of course are "the most
convincing evidences of this beauty"). As a corollary, by the time
when you defend your PhD, you loose your human nature: you become a
robot, who cannot distinguish useful things from useless things,
beauty from deformity, and decency from dishonesty. Because
questions like "why is your science useful" -- you treat as an
invitation to bewilder the interlocutor by your professional skill.
My reproach to mathematical society is that there is no culture here
in such discussions. Mathematicians do not acknowledge their duty to
explain simply and clearly why their field of interests is useful.
Gradually they turn into sportsmen whose aim is to impress the
audience by their skill, and nothing is important besides the skill.
Those counterexamples by Enflo and others are indeed quite
sophisticated. But if we treat them as progress in science, like
people in TVS do, this becomes a speculation. Because in fact
counterexamples are evidences of failure.
That is my point.
If you live in the West this problem, I suppose, is not of current
importance for you, because you may have a lot of possibilities to
change your company and to find like-minded persons, but when you live
in a country like Russia, you become completely dependent on the
opinion of those "hyper-specialists", or perhaps we should say,
"skilful swindlers"? :)
So still I am curious if there are any specialist in the theory of
topological vector spaces, who could explain these oddities in their
science?
tc...@lsa.umich.edu
<s.s.a...@gmail.com> wrote:
>Mathematicians do not acknowledge their duty to explain simply and
>clearly why their field of interests is useful. Gradually they turn
>into sportsmen whose aim is to impress the audience by their skill,
>and nothing is important besides the skill.
I agree that this kind of abuse is bad and should be fought, though I do not
see it as the same thing as hyper-specialization. Even if a subject has
connections to other fields, that doesn't automatically make it interesting
and beautiful and important. You as a student may still not be convinced
that it is a beautiful and important subject, and powerful experts may still
abuse their power to force others to accept their point of view. It seems
misguided to me to lay the blame on lack of connections to other fields
per se, rather than on the abusive behavior of the people in question.
More interesting to me is the question of whether it's a sign of bad health
when a field becomes dominated by the construction of counterexamples. I
think it certainly can be a bad sign, but even here I would be wary of
over-generalization. Note that people usually don't complain if a subject
contains lots of *examples*. But what makes something a counterexample
rather than an example? It usually means that our naive intuitions about
the subject are wrong. Some areas of mathematics may be particularly
counterintuitive, so that we need an unusual number of (counter)examples
to correct our intuition and map out the conceptual landscape properly.
Devoting a period of time, even a rather long period of time, to building
these counterexamples may in some cases be exactly the right thing to do.
Of course, if the goal shifts from trying to understand natural mathematical
structures to demonstrating one's virtuosity, then something has gone badly
wrong. But again, this can happen in any field, specialized or not.
s.s.a...@gmail.com
Tim, nobody is going to over-generalize here. Stephen wrote about
Banach spaces, where “almost all plausible conjectures have some very
horrible counterexamples”. But, as I told, the situation in the theory
of TVS is even worse. And this is not because God destined it to be so
(you can make an impression of this in my paper).
Of course, when you study a system of axioms, you have to consider
hypotheses, and often it turns out that your hypotheses are wrong,
because there exist counterexamples. But a sane person understands in
this situation that if the number of counterexamples exceeds a
reasonable level, then this means that something is wrong in his style
of making mathematical investigations: he should either change his
axiomatic system, or bound the class of objects or do something else
to reduce the number of deformities.
But those people do not understand this: every next counterexample
they boost as a “great progress in science”. As a result, those
“scientists” ruin algebraic intuition without suggesting anything in
turn.
They justify this approach by their skill: since it is very difficult
to build all those counterexamples, we should admire of them. But it
is much more difficult to build a theory where those ugly
counterexamples do not appear, why do not we think about this?
By the way, I have also been meaning to ask somebody if there is a
regular procedure to settle disputes between Western mathematicians?
Suppose somebody steals my result, or writes that I steal somebody’s
result, or my comparison with “skilful swindlers” hurts somebody, or
something like that happens. How can we understand who is right in
this situation? To which address I (or my opponent) can send a
complaint, or how do Western mathematical society expect me (or him)
to act in this situation?