Colegas,
A proposito da discussao sobre estatistica que acontece na lista,
mando dois textos, ambos do boletim do Institute of Mathematical
Statistics deste ano. O primeiro e' de Terry Speed, do depto de
estatistica de Berkeley que escreve toneladas de artigos de estatistica
e de genetica (como Fisher). O outro artigo e' uma resposta ao texto
de Terry Speed por um um pesquisdor bem mais jovem, do Canada,
que expoe uma visao muito interessante.
Renato Assuncao
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IMS Bulletin, Volume 36 - Issue 2, March 2007
Terence?s Stuff: The Big Problem
This month Terry Speed is wondering whether he? and statisticians in
general? should have more of A Vision?
About a decade ago, someone asked me
?What?s your vision?? Many things ran
through my mind as I framed my reply.
I thought about the image problem
George H. W. Bush, the 41st
President of the USA, had with ?the
vision thing? (people thought he lacked it),
then thought about the dictators, despots
and mass murderers of history who usually
had visions, but wholly undesirable ones,
and finished by repeating a small personal
joke to myself, envisaging the headline
?Statistician cures cancer!? Resisting the
temptation to reply, ?To cure cancer? ? my
questioner was not someone to be trifled with?
I replied honestly, ?I don?t have a
vision: I?m a statistician.?
I explained that, mostly, we statisticians
assist others to fulfil their visions, and
through doing that, we make our contribution
and get our satisfaction. At least, I said,
that?s how it was for me, and, I think, many
others. I went on to explain that we can?t
anticipate where our skills might be needed
next, and that I felt it was important that
we remain open to assist people as the need
arises, without trying to pick winners, and
without getting unduly wedded to a particular
body of techniques.
I didn?t say at the time something else I
believe: that in my view most statisticians
shouldn?t aspire to get into the driving seat,
to lead the research generating the data they
are analyzing; they should be happy with
a subsidiary scientific role (which is not to
say they shouldn?t expect to be treated as
equals in the research enterprise). I like to
collaborate wherever possible with first-rate
scientists, and if I?m also playing the role of
the scientist, then that pretty much guarantees
that as a statistician I?m collaborating
with a fourth- or fifth-rate scientist, for
most of us could aspire to no better than
that. A rare few of us might get to be thirdor
second-rate scientists. (This is a variant
on the saying that a lawyer who defends
himself has a fool for an attorney and a fool
for a client.)
I know that not everyone agrees with
my view on this matter, and recently I?ve
started to think I?m wrong in not having a
vision. Perhaps it?s a delusion brought on
by age that I?m moving up from fifth- or
fourth-rate in my understanding of the
science on which I work, to third-rate, and
so capable of adequately judging the science
in my projects. Or perhaps it is a different,
age-related phenomenon: the desire
to try to do something really worthwhile
before passing from the scene. Either way,
I?m wondering again, more seriously this
time, about that headline, ?Statistician cures
cancer!? Of course, it doesn?t have to be
?cures cancer?; it could be ?ends poverty? or
solving some other Big Problem.
Statisticians curing cancer has become
a more interesting?dare I say plausible??
idea than it previously seemed. As
part of epidemiology, statistics has certainly
played an important role in identifying
risk factors for cancer, the link between
cigarette smoking and lung cancer being a
familiar example. Statistics has played a very
large role in comparative cancer studies: just think
how many randomized controlled trials have
been conducted over the years, how many
Kaplan-Meier curves have been drawn,
and how many Cox models have been fitted.
However,
my wondering whether a statistician might
indeed cure cancer is not related to these
familiar examples of the use of statistics
in cancer studies, but to a more recently
demonstrated possibility: that statisticians
might learn how to interpret large bodies
of experimental data, and figure out how
to ?personalize? the treatment of cancer. It
seems to have become a truism these days
that most cancers have a degree of uniqueness
which is highly relevant to their diagnosis,
prognosis and treatment. The current
treatment for stage 1A lung cancer patients,
say, may be ineffective for up to a third
of these patients, but the problem right
now is that we don?t know which third of
them need to be treated differently, or how
this third should be treated. This situation
seems set to change. Using genomic and
proteomic assays, it is now possible to collect
large amounts of data on tumors which
capture the uniqueness of each patient?s
cancer. The challenge is to develop targeted
therapies, which recognize and attack the
vulnerable features of each cancer, and the
statistical analysis of these large amounts of
data will play a key role in responding to
this challenge. There are already promising
signs that this approach will work, and if it
does, statisticians will indeed have
helped cure cancer. What?s your vision?
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IMS Bulletin, Volume 36 - Issue 7, Aug/Sep 2007
Bertrand Clarke, University of British Columbia, responds to
Terry Speed?s March 2007 column with his ?vision for statistics?
In the mad, headlong rush to apply
existing statistical methodologies, the
development of a greater vision for
statistics is being ignored. It is not that no
unifying vision is possible. Instead, the conceptual
base of statistics?what Terry Speed
would mean by ?vision??is devolving to the
view that statistics derives its importance
from its ability, firstly, to resolve existing
data analytic problems in the present, and
secondly, to resolve inferential problems
from other fields.
Recently, Terry Speed has written of
this view approvingly. I like Terry, and he
makes a good case. However, I denounce
the implications of his view. The core ideas
of statistics are deep and important in
themselves, apart from their applicability.
They are worthy of independent intellectual
development purely because they are fundamental
to our understanding of the human
experience?the way each of us interprets
the stimuli the world puts upon us through
our senses, and through our awareness more
generally. Everyone who does not understand
the basics of statistics will suffer in
proportion to their ignorance.
In this, I see statistics as taking its
natural and primary place in the intellectual
firmament. Like mathematics, history, and
other fields, the intellectual domain of
statistics is worthy of resources and development
because it helps us understand our
world and society in aggregate.
Let me be crystal clear: applications are
important and necessary, but secondary to
the intellectual achievement of elucidating
statistical thinking. The importance of
applications in statistics derives from developing,
as opposed to just using, statistical
techniques and ideas. In particular, much of
the application of statistical techniques and
ideas in service to other fields is important
to those fields, but not to the development
of statistics. The natural test of whether
an application of statistics is important to
statistics as a field is whether or not another
statistician who is not interested in the
topic of application would still find the
work interesting. Resources from statistics
proper should not be diverted to the intellectual
development of other fields when
our own is equally (or more) deserving.
What vision do I champion? I call it
a Coordinating Theory for Statistics. I want
statistics to have a focal unity, like Newton?s
laws for classical physics, or evolutionary
theory for biology. I despair of such
a strict unity for statistics, so I call it a
Coordinating Theory because I believe the
seemingly disparate ideas of statistics will
admit a structure, more like a roadmap
than an axiomatization, so that the plethora
of core statistical ideas will be clearly
inter-related. That way we can, in a word,
coordinate their use and study.
First, some history. Statistics did have
half a vision prior to the mid-nineties. It
was all that material about foundations and
asymptotics, chiefly in the parametric case
but including classical non-parametrics as
well. In the context of this vision, people
debated core issues. Within the context of
decision theory the clashes of asymptotics
vs. finite sample properties, Bayes vs.
Frequentist vs. conditional inference, and so
forth, were evidence of a vigorous academy
leading with new ideas. They were also great
fun. However, few outside statistics cared
much.
Come the mid-nineties, that half-vision
died as computational techniques, few
invented by statisticians, came into the
field. We started playing catch-up to computer
science. Now we have another halfvision:
statistics as handmaiden to the other
sciences. These days, in fact, many journals
will only publish manuscripts which can
purport to be motivated by the detailed
analysis of a specific real data set. This
includes the requirement that computations
be feasible and user-friendly, even to nonstatisticians.
This is tuned into the wants of
other sciences and society in general.
It?s useful in many important ways.
Unfortunately it means much slower
development of the actual field of statistics.
Thus, many fields within statistics are lagging
rather than leading. Lagging not just
compared to where they would have been
had they focused on statistical development,
but also in comparison to other fields like
computer science and engineering whose
intellectual importance is growing at our
expense. However, supporting other fields
encourages people to like us, and we like
that.
Neither of these half-visions is entirely
satisfactory. The main flaw in the earlier
vision was that it did not respond well to
emerging classes of problems, and was not
tied in to the broader intellectual world.
The main flaw in the current vision is that
it forgoes independent intellectual development
of our own field; it is a subsidiary
role. Like it or not, seeing ourselves as a
support to other fields means we give up
intellectual equality with them: we cannot
be leaders. Often we will not even be
respected (consider the typical attitude of
the ?master? to the servant).
My notion of a Coordinating Theory is
an effort to complete these two half-visions.
I want to base it on model uncertainty and
predictive optimality because these two
ideas seem to me to be unique to statistics
and they are central to the other ideas that
are unique to statistics, such as hypothesis
testing, parameter estimation, and physical
modeling. Model uncertainty is chiefly
the theoretical side of my vision (though
applied researchers are often exquisitely
sensitive to it) as is the optimality part of
prediction. The prediction itself is the primary
application-oriented side of my vision.
Prediction is the key way to ensure that
statistics regularly appeals to the measurable
world. Prediction is a weaker criterion than,
say, model identification and hence more
basic.
What core ideas do I want a Coordinating
Theory to coordinate? Obviously, it
should include a formulation of the prediction
problem. Then, it must include some
measure of randomness, some characterization
of model uncertainty (if only an SE for
a parameter), and some evaluation of how
well predictions match outcomes e.g., a
cumulative predictive error.
Only slightly less obviously, a Coordinating
Theory should have a place for signalto-
noise ratios, components of variance,
large sample properties, and sensitivity
analyses for each of the model components.
I?d like to include the prequential principle
and a generalized variance bias formula (so
that components of bias and variance can
be assigned to different model elements).
There would need to be some way for the
sequence of prediction errors to update the
elements of the prediction problem and
therefore the predictive strategy. Then, a
routine way to convert predictors to estimators
and deal with dependence structures
among the data points and covariates would
round out my initial list.
To be more thorough, I?d add computing
and high-dimensional problems, even
though both are implicit in my initial list.
Did I say this would be easy? No. It will
be hard?but well worth doing. The best
applied contribution is a good theory.
Frankly, I hope some kind of a
Coordinating Theory will be developed,
generally accepted, and then become
entrenched in statistics. That way, it can be
challenged and surpassed by future thinkers.
Thus will statistics have the independent
intellectual development its ideas merit.
Statistics should be a Promethean field,
not a lagging field. We should be presenting
our new ideas to others, not doing
their analyses for them?unless we get the
main intellectual benefit from it. After all,
statistics is a compelling field dealing with
the most important questions; we shouldn?t
be afraid to shake people up with our new
ideas, or to demand they make efforts to
understand them.
I?d like to see us get to the point where
we hand over our ideas and techniques to
other sciences and humanities so they can
do the routine implementation, debate
the results, and use our ideas as a reference
point for their own development. In this
way we could turn our attention to developing
more new ideas so the beat goes on.
The only way we can do this is to pursue
the central ideas that animate statistics
proper, not getting sidetracked into solving
problems for other people. Let us have the
confidence that our contributions, theoretical
and applied, can stand on their own
intellectual merits.