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Supporting Fundamental Innovation

Most of the funding of research efforts I've been involved in since ARPA-Parc have been with various profit making companies -- Atari, Apple, Disney, HP, SAP, Infosys, etc. And there have been various kinds of compromises involved. And some good work on smaller scales did get done. Others of my colleagues in the diaspora that started in the early 80s wound up at Microsoft, DEC, IBM, Bell Labs, etc.

These same people with the same big ideas, talents, more skills and knowledge, and energies, were not able to muster the critical masses of "psychic resources" that are needed to get to the "other worlds" places that were routinely the province of the smaller but "felicitous" and longer range resources of ARPA-Parc.

Bell Labs is a great alternate example. Before the divestiture it was a fountain of qualitative advances -- afterwards, it couldn't get out of its own way -- most of the good people were still there, but the management contexts changed.

I once gave a talk to Disney executives about "new ways to kill the geese that lay the golden eggs". For example, set up deadlines and quotas for the eggs. Make the geese into managers. Make the geese go to meetings to justify their diet and day to day processes. Demand golden coins from the geese rather than eggs. Demand platinum rather than gold. Require that the geese make plans and explain just how they will make the eggs that will be laid. Etc.

I had quite a few more, and most thought it was a funny talk. (Oscar Wilde once said "If you want to tell people the truth, make them laugh or they will kill you".)

But only a few in those Michael Eisner days of Disney in the late 90s realized that they should just let the geese lay the eggs. Someone else can make the coins. Someone else can buy platinum with the gold. Someone else can manage. And so forth.

Most of these kinds of misunderstandings are because many people really want other people to be like them, and they want to be able to use what they would do to ask others to do, etc. It was harder to explain to the Disney execs -- and many potential contemporary funders -- what the golden age funders understood full well. Namely, the reason they are the funders is because they did something that got them in control -- in one way or another -- of money. Meanwhile, the people who should be funded were spending their time getting deeper and better at their arts.

A small amount of compromise is possible, and it is even needed with great funders. But there's no question that Parc would have failed if Bob Taylor hadn't forced Xerox to sign a legal agreement that they had to keep their hands completely off -- in all ways -- whatever we decided to do for the first 5 years.

This was the right ploy because -- as Dave Evans used to pound into us in grad school "You can't lie to funders to get funding and still do good science".

As I tried to explain in the two Stanford Lectures I did for Sam Altman's "Startup School", the "dynamics of the qualitative" and the "dynamics of the trillions rather than the billions" are completely different from the dynamics of startups, and especially for the majority that are incremental.

The "zeitgeist" of ARPA-Parc stretches back to the WWII musterings of scientists and engineers, much of it fostered by Vannevar Bush. One of the things they learned how to do was to "do Art at scale". The ARPA funding by Licklider starting in 1962 carried that context forward into computing, and the results speak for themselves. It's not that it is the only way to do things -- but it is at present the only way *known* that produces the big results.

This all sounds very delicate. Especially compared to the normal business/commercial processes.

After more than 50 years of doing edge of art research, my conclusion is that "it *is* delicate". An important part of any art is for the artists to escape the "part of the present that is the past", and for most artists, this is delicate because the present is so everywhere and loud and interruptive. For individual contributors, a good ploy is to disappear for a while. What was wonderful about the big creative projects of the golden age was that they had to be conducted out in the open by lots of people, but the processes and pressures were such that the delicate parts were not done in.

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Here is one perspective. The "golden age" funding included a lot of funding for "problem finding" -- which means the funders were not vetting specific proposals or funding "directed research". The points of agreement were on a "vision of desired future states", not goals or routes. An example of the vision was Licklider's "The destiny of computers is to become interactive intellectual amplifiers for all humans, pervasively networked world-wide". This vision does not state what the amplification is like or how you might be able to network everyone in the world.

One way to characterize this in modern terms is that the golden age funding was like "MacArthurs for groups". The people chosen for a MacArthur Fellowship get $125K annually for 5 years with the only vetting being a bet that the person will continue to create. The golden age funders gave the equivalent in today's dollars of several million dollars a year for five years to about 20 principal investigators so they could set up groups (much of the fundamental creative work in computing requires 8 or more people working together).

The assumption by the golden age funders was that some of the special people they were funding would be able to come up with good goals and methods, and that a "baseball percentage" of successes (batting around .350 say) by top people would be enough to make the vision happen.

I was used to being funded that way in the ARPA-IPTO years, but later had to scratch more and more to get funding enough for groups around me.

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Parc was "effectively non-profit" because of our agreement with Xerox, which also included the ability to publish our results in public writings (this was a constant battle with Xerox). In the end, all the technologies got out in useful ways. ARPA was non-profit, but had many commercial spin-offs, and this was regarded as "the way things should be" to get things out in the world in quantity. Really fundamental inventions are too large for single human organizations to deal with -- what one wants is a reasonable balance between what is freely shared, and how things can be made from them. Finding these balances in business has always been a challenge. It seems very difficult for most business people to notice the amounts of larger cooperation and sharing needed for them to be able to do any business at all.

Socrates didn't charge for "education" because when you are in business, the "customer starts to become right". Whereas in education, the customer is generally "not right". Marketeers are catering to what people *want*, educators are trying to deal with what they think people *need* (and this is often not at all what they *want*). Part of Montessori's genius was to realize early that children *want* to get fluent in their surrounding environs and culture, and this can be really powerful if one embeds what they *need* in the environs and culture.

By the way, this syndrome has been killing NSF funding in computing for many decades. They require in their proposals an explanation of how one is going to "solve the problem", and this has effectively filtered out all but engineering type proposals (some of them have been good -- but most of the stuff that needs to be done requires funding for "problem finding" and NSF -- for fear of Congress -- has been unwilling to do this).

Another way to think about this is as a confusion with what kinds of reasoning that is needed when the funding is for "art". The MacArthur people have seen that they need to "fund ahead" for the Fellowships -- but their "100&Change" program is all about requiring the applicants to say how they will solve the problem (this limits the scope of what can be taken on).

Yet another perspective is to note that one of the human genetic "built-ins" is "hunting and gathering" -- this requires resources to "be around", and is essentially incremental in nature. It is not too much of an exaggeration to point out that most businesses are very like hunting-and-gathering processes, and think of their surrounds as resources put there by god or nature for them. Most don't think of the resources in our centuries as actually part of a human-made garden via inventions and cooperation, and that the garden has to be maintained and renewed.

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Licklider "just funded" period.

As I pointed out in a previous email, Engelbart couldn't get funding from the very people who made fortunes from his inventions.

It strikes me that many of the tech billionaires have already gotten their "upside" many times over from people like Engelbart and other researchers who were supported by ARPA, Parc, ONR, etc. Why would they insist on more upside, and that their money should be an "investment"? That isn't how the great inventions and fundamental technologies were created that eventually gave rise to the wealth that they tapped into after the fact.

It would be really worth the while of people who do want to make money -- they think in terms of millions and billions -- to understand how the trillions -- those 3 and 4 extra zeros came about that they have tapped into. And to support that process.

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The Parc money came from Xerox, the ARPA money came from DoD via the Cold War, but was unfettered and in the public domain. The most important difference between the "Golden Age" funders and those of today, is that the former didn't confuse responsibility with control -- they were responsible but they knew that the researchers had to control the choice of projects and methods. The funders of today -- most particularly the tech billionaires, but also execs in companies, bureaucrats in DARPA and NSF, etc -- think that they have to control. This winds up with bad choices for goals and projects, and bad processes. The "Golden Age" funders "funded people, not projects".

If "good funding" were to come from the pop culture, I wouldn't turn up my nose at it (nor would any of my past colleagues). The main aim is to make qualitative improvements in the human condition. I think everyone would agree that making a billion dollars does not qualify a person to play professional sports, nor to be a classical violinist. Nor does it qualify a person to be able to direct fundamental research. These are all deep skills that anyone with a billion can learn, but if they don't learn them, then having them deep in the loop is a real problem for progress.

by Alan Kay

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