
After discussing Tom Wolff's (n+2)/2 Kakeya result, I made the comment
"However, there appears to be a limit to what can be achieved purely by
applying elementary incidence geometry facts and standard combinatorial
tools". The reason for this comment is as follows. In R^3,
Tom's result gives a lower bound of 5/2 for the dimension of Besicovitch
sets. This argument, and any other argument which uses as its fundamental
ingredients incidence geometry and combinatorics, will also work for the
complex analogue of the Kakeya problem in C^3, giving a lower bound of
5 for the real Minkowski or Hausdorff dimension of such sets. However,
this bound of 5 is in some sense sharp for the C^3 problem, as the Heisenberg
group {(z_1, z_2, z_3): z_3 = Im(z_1 \overline{z_2})} has 5 real dimensions,
and contains a 4realdimensional (or morally 2complexdimensional) family
of complex lines, and thus almost qualifies to be a Besicovitch set example.
(Admittedly some of the lines in the Heisenberg group example are parallel;
however, this shows that one must use the nonparallelness of the line
segments in a nontrivial way in order to surpass 5/2, at least in the
context of the complex field (or any other field which contains a subfield
of half the dimension). In particular, arguments which are based
solely on incidence geometry (which cannot easily distinguish between parallel
and nonparallel lines) are extremely unlikely to improve upon Wolff's
bound. (Further discussion can be found in my paper with Izabella
Laba and Nets Katz here).
I elected not to include the above detailed explanation in the Notices
article as it was rather technical and could be viewed as a gratuitious
reference to one of my own papers.
In discussions with Tom Wolff in 1999 it was clear that Tom was
already aware of this fundamental limitation to the geometric method.
To escape this limitation there are essentially only two routes.
The first is to exploit the nonparallelism of the line segments, as per
the arithmetic approach pioneered by Bourgain. The other is to use
the structure of the real field to show that, unlike the complex field,
R does not contain a subfield (or any similar object) of dimension 1/2.
This latter type of approach (together with other considerations) led Tom
to other closely related problems in geometric analysis such as the Falconer
distance problem and the dimension problem for sets of Furstenburg type.
These problems deserve further attention and may well be the key to further
progress in the field; indeed, Tom appears to have already seen this in
his survey article for the 1996 Prospects in Mathematics conference.
A (rather technical) paper of Nets and myself continuing an exploration
of these issues can be found here.
In trying to make the point about the limitation of the geometric method,
I had the unintentional effect of appearing to dismiss Tom's landmark (n+2)/2
paper as mere "elementary incidence geometry and standard combinatorial
tools". This was not the desired impression I wished to give at all.
In fact, I hold to the (perhaps paradoxical) opinion that some of the best
and most beautiful papers in mathematics are those which use extremely
elementary observations in an unforeseen way to yield progress on a problem
which was otherwise thought to require much more sophisticated and technical
arguments. Tom's (n+2)/2 paper does, in my opinion, fall into this
category, although Tom also introduced valuable technical devices in this
paper as well, such as the systematic use of pigeonholing, the hairbrush
construction, and the twoends reduction. It would have been nice
to discuss these tools in the article as well but I could not see a way
to do this given the space provided and the nonspecialist nature of the
readership, and so I concentrated instead on the ideas of Tom's paper which
could be easily grasped by nonspecialists. (My coverage of the arithmetic
arguments of Bourgain and Gowers were also in this vein). It is also
remarkable, given the rapid progress in the field, that Tom's paper, now
6 years old, has only barely been surpassed in the threedimensional case
(with a very small improvement of 10^{10} in the Minkowski problem, no
improvement in the Hausdorff problem, and an xray refinement only in the
maximal problem). Some idea of how difficult it is to improve upon
Tom's results in the lowdimensional case can be found in this
paper. Despite being one of the authors of this paper, I have
the opinion (which appears in the Notices article) that the techniques
in this paper are also "clearly insufficient to resolve the full conjecture".

The oscillatory integral section, which focusses on Fefferman's negative
result on the disk multiplier and on the BochnerRiesz problem, is not
intended at all to be an exhaustive survey of the vast topic of oscillatory
integrals. This section in particular suffered from the space restriction
of the Notices article; for instance I would have loved to devote much
more space to the restriction problem, and in particular to the TomasStein
theorem and its variants and improvements. (Indeed, in the original
longer version of the article I devoted more space to the TomasStein
theorem and the closely related Strichartz estimates for dispersive and
wave equations). There are also a number of other results of similar
flavour to Fefferman's results (using Besicovitch sets to yield unboundedness
results in harmonic analysis) which also appeared in the 1970s, but I chose
to focus the reader here on one specific result (Fefferman's) rather than
a broad array of results. For similar reasons I focussed the discussion
of the BochnerRiesz problem on those results which were specifically connected
to the Kakeya problem or to PDE; as such, I did not devote much space to
other important, but more technical and less relevant to the KakeyarestrictionBochnerRieszlocalsmoothing
axis of conjectures, BochnerRiesz results such as maximal or weighted
inequalities or to the behaviour at or above the critical index (n1)/2.
I hope to do fuller justice to this aspect of the field at a later date.

In the PDE section I discuss the local smoothing conjecture, arguably the
most difficult of all the conjectures in this field, and then state "This
conjecture is far from settled; even in two dimensions, the conjecture
is proven only for p > 74 (due
to T. Wolff), and at the critical exponent p=4 the conjecture is only
known for \eps > 1/8  1/88 [TaoVargas],
[Wolff]".
Once again, this sentence could be misconstrued as an attempt to belittle
the work of Tom, Ana, and myself. Actually, the intent was to highlight
the extreme difficulty of this problem, in that even a mathematician of
the stature of Tom Wolff , attacking the problem on two different fronts,
was only able to achieve a modest amount of progress on both (though even
this amount of progress would have been beyond many lesser mathematicians
such as myself). In fact, I rate the two papers of Wolff cited above
as two of the most impressive papers I have ever read. They share
a common theme, in that they invoke a powerful new technique, namely induction
on scales. Prototypes of this idea have arguably appeared in
earlier papers by Bourgain (and to some extent in the work of Ana Vargas,
Luis Vega, and myself) but Tom was the first one to demonstrate (twice!)
that this technique can be used to obtain nearlysharp results on extremely
difficult problems. In the original
longer version of the article I spent a great deal of space describing
this technique, as I believe it is one of the most exciting recent developments
in the field (as it is seemingly the only tool we have that is capable
of giving optimal results, as opposed to small fractional improvements
on existing bounds). Unfortunately the referee and the editor decided
that this material was somewhat technical, and made the article too long
for the Notices, and so my commentary on the induction on scales technique
was compressed to a halfparagraph which does not do the idea justice at
all. I have attempted to describe this idea more fully in some other
unpublished expositions (one
on Wolff's bilinear cone estimate, and the other on
Wolff's local smoothing estimate).