Chronology Current Month Current Thread Current Date
[Year List] [Month List (current year)] [Date Index] [Thread Index] [Thread Prev] [Thread Next] [Date Prev] [Date Next]

Re: how to judge creative ideas (was: barometer parable)



Hi all-
Michael and John are arguing two extremes of an issue that has a continuum
of possibilities. Given a finite budget (I use "budget" in a much broader
sense than available dollars), the issue I propose is: What fraction of
my resources should I "waste" on research with no foreseeable use. When I
did a brief stint at Texas Instruments in the early '50's I heard the
figure of (I think) 2% expressed as the policy of the company. I don't
know that there is a credible analytical way to answer the question.
Regards,
Jack




On Sun, 9 Jun 2002, John S. Denker wrote:

Michael Edmiston wrote:

(1) I'm not as confident as John seems to be that we can or should
categorize things as having long-delayed or long-enduring impact. It seems
to me that all "basic research" is long-enduring. Anytime we gain new
knowledge that knowledge exists forever unless it is later found incorrect.

I've seen lots of stuff that was called "basic research" that
was worthless, is worthless, and will remain worthless for all
time.

If I throw a barometer off a tall building, it wastes the
barometer, and the value of the "scientific" information
obtained in the process will never (and I mean NEVER) repay
the cost of the barometer, especially when since the information
could have been obtained in other ways.

I suppose if very few people cared about the new knowledge (at the time it
was acquired) then it could get forgotten. However, we're pretty good at
publishing research in searchable libraries, so all knowledge ought to be
long lasting short of wars or other disasters. Once we admit that basic
knowledge is long enduring then each new piece becomes one of the links in
John's chain that eventually becomes a useful product (beyond the usefulness
of pursuit of knowledge as good for the human endeavor).

Long-delayed impact has very little Net Present Value, because
of the exponential discount factors. Something that "eventually"
becomes part of a useful chain might still have a negative NPV.

Suppose I buy a bond costing $100.00, which promises to pay back
$0.01 per year forever, starting 100 years from now. The payback
in nominal dollars is infinite, because forever is a long time.
But still it would be an incredibly foolish investment. There
are much better investments available.

We live in a world with finite resources. Whenever you spend
resources on something with unduly long-delayed payback, you
are taking resources away from something with greater NPV.

I am curious if John would have funded the early NMR research in the mid
1940s. In the beginning it was just "basic research" in a physics lab.

It was obvious in the 1940s that NMR had commercial impact.
http://www.varianinc.com/cgi-bin/nav?varinc/docs/corp/history

... It
took about 30 years between the original basic research and the first work
aimed at producing images. Then it took another 10 to 20 years for MRI to
be a commonly used technique (depending on what one wants to define as commo
n).

Some imaging was done in the 60s. Maybe earlier; I'm not an
expert. It didn't become "common" until there were powerful
computers to invert the data from the frequency domain to
real-space domain.

IF (IF!) imaging were the only application of NMR (which is most
assuredly not the case) then yes, I would have kept funding
for NMR at a very low level during the 40s and 50s and maybe
the 60s, until somebody could tell me a plausible story about
how the image-processing was going to be done. And (in this
assuredly imaginary situation) that would have been the right
thing to do. It would have freed up funds that I would have
invested in something else, thereby putting me in a stronger
position to fund the NMR work when the proper opportunity
came along.

In a world run by the business model, basic-NMR research to today's MRI
would be an incredibly long-delayed payoff. But it happened because the
knowledge was long enduring and we eventually figured out some uses for it.

This is fallacious for two reasons. Saying NMR is valuable
"because" it had a long-enduring impact is like saying
human beings are smart "because" they walk on two legs.
First of all, it doesn't fit the facts. Chickens walk on two
legs, but they're not very bright. Secondly, even if
chickens were smart, it wouldn't prove that two legs is
the _cause_ of the intelligence. The circus trains dogs
and bears to walk on two legs, but that doesn't automatically
make them rocket scientists.

Let me decode the meaning of the analogy: You may be able
to find some things that are valuable now that were invented
a long time ago "as a lark". But there are not nearly as
many such things as most people suppose. Selecting the
data _a posteriori_ is highly unscientific. And secondly,
even if there were many such things, it wouldn't support the
notion that investing at random, without regard to payoff,
is a good investment strategy. Maybe people made bad
investments back then; that doesn't require us to make
bad investments now.

In John's definitions, long-delayed impact is bad, and long-enduring impact
is apparently a little bit better.

That's not quite what I said.
-- Ideally you want prompt _and_ enduring impact.
-- You can do OK if you have a prompt but temporary impact,
if the impact is big enough while it lasts.
-- If the impact is long delayed, being long enduring won't
save it, unless the magnitude is astonishingly large.
Those exponential discount factors are brutal.

I would say that all basic research has long-enduring impact

I've seen lots of long-enduring worthlessness.

and I view this a very good.

I strongly disagree.

... John seems to downplay
this type of incredible impact because anybody can use it to justify just
about any kind of research.

Yes, that's one of the big reasons why I object.

I admit I can be somewhat arrogant and state
that basic physics research is more likely to lead to unanticipated
magnificent impacts compared to a study of the nesting habits of some
obscure bird. But then I remind myself that some people think the nesting
habit study is very interesting, and if they want to pursue that, and even
manage to get some funding for it, then more power to them.

It would be incredibly arrogant to say that just because
I'm interested in XYZ, the taxpayers should fund me to
study XYZ.

Physics generally has a better track record than many of
the "soft science" or "engineering" fields as measured
by uncitedness
http://www.garfield.library.upenn.edu/papers/hamilton2.html
(which is of course an imperfect way of measuring things).

But I claim that is because a goodly number of physicists
over the years have not adopted the supercilious approach
Prof. E. seems to be advocating, but rather they have chosen
to work on things that have a fair chance of being useful
on a realistic timescale.


--
"But as much as I love and respect you, I will beat you and I will kill
you, because that is what I must do. Tonight it is only you and me, fish.
It is your strength against my intelligence. It is a veritable potpourri
of metaphor, every nuance of which is fraught with meaning."
Greg Nagan from "The Old Man and the Sea" in
<The 5-MINUTE ILIAD and Other Classics>