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Re: how to judge creative ideas



Michael Edmiston wrote:
...
* * * Inconsistencies * * *

I don't understand how John can say...

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. (John Denker)

after he already said...

Somebody has to create one isolated piece, and
then another, and then another. More
often than not, the pieces are created in no
particular order, and we have to collect quite
a few of them before we can start linking anything together.

The research world would be crippled if researchers
were required to build every chain in order, link
by link. It is extremely common for pieces to be
invented in isolation, and linked up only later. (John Denker)

It seems to me these are contradictory.

I don't see any contradiction.

Doing something totally useless "on a lark" is very
different from doing something that will (with reasonable
probability) be usefula bit later, once the other links
in the chain are produced.

Also, John referenced a nice historical sketch of NMR at the Varian website.
John said "It was obvious in the 1940s that NMR had commercial impact."
Obvious to whom, and when? The Varian site says, "Both Bloch and Hansen
viewed their work as an advance in physics theory with little or no
immediate commercial value and thus it was the suggestion of Russell Varian
that a U.S. patent application be filed to cover this work." This says to
me that Bloch and Hansen had no "practical benefit" in mind, and they would
not have stated any such rationale in any funding proposals they might have
made. Russel Varian could not have seen the commercial value if Bloch and
Hansen hadn't done the work motivated by intellectual curiosity.

To that I say the world would be better off if the likes
of Bloch and Hansen would spend a little more time thinking
about the practical benefits. It costs a little extra to
bother with real-world issues, but the benefits are large,
out of proportion to the costs.

Also, at the Varian website, the sputter-ion vacuum pump is described and it
says "At the time of its development." Recalls Helmer, "there were a lot of
people at Varian that were not convinced of the practicality and
marketability of Vaclon pump technology." Further text at the website makes
it pretty clear that Varian almost abandoned development of this pump, yet
it turned into one of the big success stories for Varian.

I don't see any inconsistency there. I said the trick is
to run risks wisely. To say people "were not convinced" is
to say that they saw it is a risk. Fine. That's expected.
Good researchers run risks all the time, risks that would
cause ordinary mortals to instantly die of adrenalin poisoning.
The risks don't pay off 100% of the time. That's why there
are P(...) probability factors in the NPV equation. The
only requirement is that the risks pay off often enough,
and pay off big enough, that you win on average.

Also, at the Varian site, with respect to NMR, it says, "As is often the
case with basic discoveries in science, the original intent of the work
turns out to have been far afield from the ultimate practical application."

There's a lot of truth in that. The wise research manager
takes that into account. From time to time one has to make
the argument that "this is almost certainly good for something,
but I can't yet tell you exactly what". That's very different
from saying "this cannot possibly be useful".

I like to talk about fishing for tuna. There are two ways
of catching tuna using hooks (we wont't discuss nets). Method
#1 is to put a piece of bait on the hook and dangle it in
the water until a tuna takes that bait and the hook along
with it. Method #2 is to throw a bunch of chum in the
water. The tuna show up in great numbers and go into a
feeding frenzy. You then dangle unbaited hooks in the water
and some of the tuna will get hooked. The accounting is
tricky, because you can't prove that a particular piece
of bait contributed to hooking a particular tuna (like you
could with method #1) but it turns out that method #2
works fine !!on average!!.

It would be stupid to spend money on chum and then not
bother to dangle the hooks. Similarly it would be stupid
to chum with arrugula or some other expensive substance
that the tuna aren't interested in.

So it is with research. The accounting is tricky. All
you can ask is that things work out !!on average!!. But
averaging doesn't give you a license to spend research
money on arrugula or other things that have no chance
of bringing you closer to the goal.

To use another analogy: In the research business, we often
speak of "hitting a home run" i.e. making a really great
discovery. It's hard enough to do that, and it becomes
impossibly hard if the researcher is required to "call
the shot" i.e. to specify exactly what part of the bleachers
the ball will land in. So do your best. Hit the ball hard.
Steer it enough that it doesn't go foul, but don't constrain
yourself to hitting a single seat. Sometimes your best
effort will result in an inglorious strikeout. Sometimes
it will be a sacrifice fly. Sometimes it will be a grounds-
rule double. Sometimes it will actually be a home run. We
will let you try a few times and take the average. But
remember, the averaging doesn't give you a license to be
stupid or lazy. Getting paid to do research is a privilege
and a high honor, given only to those who try their best
every time they come to the plate. Don't abuse the privilege.