Alan Kay Talk at Virtual Heidelberg Laureate Forum 2020

okay it's

my pleasure to introduce the next speaker of this

morning whatever depending on your

time zone it's allen k recipient

of the acm am touring award in 2003

for i quote pioneering many of

screen and go to full screen on slides

and in the upper right hand corner

is a place for your technicians to put

hey will

see what it is i hope

did the technicians get this

yes

they did and andreas

we're going to have to you're going to be in the way of the slide

so if the technicians will they can take me out

i'll be happy yes well

they yes okay

there we go

and okay

um hello everybody

uh i have a simpler bio than

the the one that they

gave you which

is just that no

his research community than i do

and that of course

was the arpa

information processing techniques office

uh in the 60s and

then xerox park which was an outgrowth of it

in the 70s

and so the simplest

uh piece of advice

i can give anybody unless

you're truly de novo

is just find a good research community

ours

benefited tremendously from

this slogan the goodness of the results correlates

most strongly with the goodness of the funders

we had i think the greatest

funders that computer science research has ever

had and so

much of what

we did and

that is idiosyncratic to

that particular research community and those

funders so i'm not going to

cover that today i've given longer talks trying to

explain this research community today i thought i'd

are maybe more generally applicable

and that would lead as quickly as

possible into our question and answer

the direction of this talk from

questions that uh

some of the junior researchers

emailed me over the last week so

you to them and some of them will

see some of their questions answered

the whole talk is really

about pondering i've divided into two parts

the first one

is just dealing with

the tyranny of

the present or the tyranny of normal

and this is an idea from arthur

kessler book

act of creation

and he says imagine our

mind as being

like a flat plane and our thought processes as being

like an ant and the

ant doesn't know it's pink

because it's the only uh color that

ever seen it can wander around it can do

all kinds of things it can find obstacles it can problem

solve uh

and every once in a while it will

have an outlaw idea

maybe in an unguarded moment

but the aunt has been to church

gone to school the aunt has

tried to get funding from a government funding agency

and so there's a big ker splat

that wipes out that little outlaw

idea get back into the pink there

but maybe the ant is taking

a shower just waking up and all of a sudden

this

outlaw idea gets much much bigger

it's a kerpal and

when one of those gets big enough

makes you see oh here's a blue

plane i didn't know that

my thinking could be more than two-dimensional

but here's a whole other world i didn't even know about

maybe i'll start exploring that and

course once you found

a an exception

to the world

that you thought was normal you realize oh there's

lots of them everywhere

there is there's a possibility escaping

and getting into a different set of thought processes

so the slogan i made up for this many years

ago is point of view is worth

80 iq points often

you are the context that you're

in uh that makes the difference

and certainly we

in our era are in

a context that was laid in the 17th century with

invention of science a lot of

what we do depended on what happened then and

years or so earlier like

leonardo was we would lack the context

to do anything with ideas like he had

another way of looking at it is from marshall

mcluhan i don't know who discovered water but it wasn't a fish

the ant doesn't know that it's

in a pink plain because it's only ever seen pink

and a question for you to ponder

while i go on with the talk if

the pink normal is sanity

because we equate normal with sanity

what then is a blue thought or a green thought

okay here's another way

to look at it uh from the

generally in school we're at

given a problem b we're supposed to

go towards it and be successful most

of the time but

in fact lots

of real problems also

exist in more dimensions

than school problems or most problems

eem to be so in the ant here doesn't

can feel gravity

can feel things are getting more difficult

but just feels the difficulty

ant has been taught well

then it will just keep on trying

it will hold on

to this particular goal in this particular way to get to

kay here's a

guy in africa he wants to

catch a baboon

so he pokes a hole in a termite

nest here

here's a young baboon

him do it wondering what's going on because he's curious

like all us primates are

and the hunter

puts some seeds in the hole

and just goes off to the side

the young baboon is thinking about this

curious

curious

better go take a look

i can smell

oh seeds

grab onto those seeds

whoops he's stuck could just let go

of the seeds but he won't let go the seeds

he's a primate just like us

he will just hold on to those seeds until

a guy comes up and catches him

now this is a cognitive

that is called a loss aversion

it's one of several hundreds of cognitive biases

that we have this is one we share with

primates this is also how they catch monkeys

in burma and

i won't tell you the rest of the story you can find this

video on youtube uh but i will tell you

hunter does not kill or hurt

the baboon the reason he caught the baboon was for a completely

different purpose which you'll find interesting

okay but what if we didn't have laws

aversion but one thing explorers

know they have a heuristic that says boy if things are really getting

tough we should at least explore around

the hill and the and the gully

there aren't everywhere

and so we might have to take a longer route around

but actually we'll get to be faster

we'll just have to travel a longer distance

and in fact

away from this goal we might even find a super

highway one of the super highways we use

today is called science

science get off to

can go much much faster

and in this case you travel longer but you get

to be much much quicker

but

you could also use

science to boost engineering and invent an

airplane and just fly over the whole thing

that takes a little time but now we've

got something that's generally useful

and even better once we started

thinking in this way we might find

one of these blue planes

and on the blue plane we might find

a goal c that is much much better than b

was and in fact if you think

about it this is

a key

to even thinking about your own schooling if you

went to college trying to

get to b and college showed you so

much that you came out with a c that you

never knew existed before the college has done its

job otherwise it's only

helped you on your own goals it hasn't helped you expand

now here's a a barn that burned

down one that burned down in the 17th

century inspired a japanese

poet to say oh the barn burned down but now

the moon was more rewarding to him

than his barn

that gives us a way to think about

how do we think about ideas do we think of

them like matter

they are separate things they collide with each

other like words or categories that have hard boundaries

or do we think of them like radiation

or light or processes or relationships

and these superpose

so it can shine all of them on the wall at the

same time and we can

there we can see interesting combinations

other they might not

be compatible directly but by

not fighting each other we can get some ideas

about what we can do with them

and guess what the the moon might actually

have been hiding all the time behind our categories

but in fact in

the radiation idea of ideas we can find

the moon and of course in

california we like t-shirts

o this is a good t-shirt for researchers and

other curious people

and again these categories

have this sense of reality

they're so well defined

they're so uh set up they've

been used so often that they actually can get

in the way about thinking about things

well here's uh kessler's book

act of creation written in the mid 60s

it has many wonderful ideas not

just this two planes intersecting

he has a whole theory of creativity

and humor and science

and many other interesting things he was

a very famous writer who later in his life turned

his hand to the behavioral sciences

and a more recent book

which has many things

to do with the way human brains actually work

by kahneman who won the nobel

economics also

with his partner tversky

uh coined the term cognitive bias

and i uh

if you look at the wikipedia article on cognitive biases

and the cognitive bias codex

find all sorts of interesting things including

the fact that you'll be able to think of more cognitive

biases than are listed there we have a

of them now if you think about it if we know what our

cognitive biases are as human beings

we should be able to create heuristics

to deal with them

think of them as dangers out in the

world we have to make up heuristics to deal with

these things okay

the second part of this

which is really part of the first part

is that generally

speaking and certainly

in my experience almost all the good stuff

that happened in my research career

of more than 50 years now

came from finding problems the problems

that were around the problems

nsf likes computer people to solve

and so forth are ones that

can be explained the solutions can be

explained so they're really more like engineering

but in this golden age

of 60s and 70s when a lot of new

stuff got done a lot of it got done because

arpa and park were willing to fund researchers

to poke their noses around

with their own conceptions of the problems

most worthwhile looking at

so you can think of it as widening context

closing your eyes

the perfume that's around

find the perfume that smells good to you

so

this context idea is interesting

we still have to explain

people the person is the first word in personal computing

why do we have to do that because the

user interfaces they do are so terrible

so they're much more interested in the computing

part than the person part but if you think about

it this is not a great term because

um humans

don't exist by themselves

out of the woods or in a cave

we most of us view that as punishment

and so what we're what we're actually

embedded in

and we can't be human without is from the time

of birth to be embedded in a

human culture and that culture

is where a lot of the

learning and attitudes and worldviews and other kinds of things

come from if we just pick

a few things that come out

of this way we can say well person is

personal computing but in fact in

a culture we have a duty to our society

we have a duty to the next generation

it's not just about us

we have to understand the world views

we have to deal with

the schooling of the next

generations and the adults that we have

today there's this idea of richness

man does not live

by bread alone so this

notion of richness this is a tough one

used to be more embedded in schools than it is now

it's one of the most important things because

it deals with things that are outside

of simple pragmatic

problems and then there's the

idea of livelihood

earning a job but it's sort of the least important

of the six that's around and these

seven things together are too

small a number but it just gives you an idea if

you just pick seven things

for a context for doing research and computing

here's seven i picked

and these are themselves embedded

in much larger issues

here are 12 big issues there

were issues 60 years ago when i started

their bigger issues today

and

these issues are actually global

so they're not tribal

they're not local cultural

there affect everybody and

the global environment is dying

in part because

many of the people who are the most active

over the last 150

years we're not concerned with

the larger environment

so if you think about a child born

year who is going to be 80

century we wonder well are they even

going to get there is there any possibility

80 years from now

for that world to be better than the one that we have

now or is it going to continue this

piral so why do i put

here because this is where

my community

in the 60s and 70s took a lot

of the romance for

the problems that were chosen they were chosen to deal with

these large issues not

just helping engineers

and we can widen this out one more

level to thinking about humanity

in general which is recently discovered

a planet many people don't really get that

a hundred years

ago the

in communication with each other and our technological infrastructure

this is a self-portrait of the internet

uh is enormous and also

large

our bodies are very

complex systems and our brains are even

more complex so if you look at these we've got

his idea

of i hope what what that caption

says there it's blocked on my screen

it says uh the systems

we uh live in and the systems

we are so we have this context

with which to get these new

and they are connected

so it's not just just that each one of them is a non-linear

complex system the whole thing is very

complicated for most people still these

are invisible they're not taught

now we can get to this

much larger view of science which by the way has its 400th

anniversary this year from francis

bacon he defined

science that we need is that we

need to have methods to get around with what's wrong with our

brains

and we will learn

thereby this is in a book called

the novum organum scientia you

can look it up

so science is about 400 years old

ating from this bacon idea

systems are less than 100 years

old and not

even taught in most k-12

curricula

couple of quotes from einstein

we cannot solve our problems with the same levels

of thinking that we use to create them

it says don't stay the big plane has

more or less ruined the planet you've got to find

a blue plane or a green plane that

has stronger thinking methods including

ways of getting the adult population

of the world to understand what's going on

and

insanity is doing the same things over and over and expecting

results that's what's been going on

london watching

europe and the united states go

through successive waves of

a pandemic which as a former biologist

can tell you has nothing interesting or

new about it from the time

they started identifying the crucial parameters

of it a country like new zealand

went with what it

actually is and prevented almost

all deaths they've only had 23

or 24 deaths whereas

the rest of the world somehow just cannot

get themselves to deal with

what's actually going on but instead they want to deal

they hope is going on and what

they hope will happen so this is a tragedy

now in the 60s the arpa community

was devoted to these

many of these ideas the climate

idea by the way goes first big warning

on the climate was 1963

by nsf so that was 57

years ago uh engelbart

uh

right here uh

was a big thinker about this and

known today it's unfortunately just known for

the mouse which he said hey that's just that's

just a button on the car radio we invented

a whole car so that's been a

real mess and what we're doing right now is absolutely

what they were doing when you see something

like what we're doing now they were actually collaborating

in groups

and i can't explain this but

you can see this demo

idea here though is that

the demo was the smallest part

the demo 168 was the smallest part

1962 engelbart

wrote a huge program

right before he was funded by arpa

and a lot of what he did can sort of

up what the whole community was about

here's the way he thought about

what you needed to do he said look

humans definitely use

tools but the problem

with the tool the problem with a hammer is it doesn't teach you

much except you can hammer things

you'll eventually use a nuclear weapon as a hammer

when you grow up so hammer learning about

hammering in a context-free way doesn't really

work and

what happens with this is that

why ends up building

rather poor heuristics

in our minds so the first thing engelbart

said look we have to have education and training

the more powerful the agencies

that humans get to control

uh the more different we have to make

reactions to them we can do that through

education and if we do that then we can use

powerful methods that have been invented over

the last 400 years and we can invent more

and we can come up with stronger and stronger ways

to represent our ideas especially now

the computer so to him this

quintuple here

was one augmentation unit the

human merged with these four

things and then the idea is

humans do that really count are

done in groups so what we want to do

is make groups of these augmented

human beings where the group itself

is augmented in a similar way so

that is a really big idea uh

doug was in despair

the last 20 years of his life

on saying doug don't worry just stay alive

they'll eventually get it and

he died and the world hasn't got it

so there isn't a system like this

except some a few specialized

ones for specialized scientists and engineers

but for the general public there's nothing like this

well let's

take a look at the world's greatest hockey player

why was he so great

hings they complained about was uh

his percentage of

getting goals was low but he got

han a thousand goals more than anybody else in history

and he said well you miss 100 of the shots

you don't take so you got to shoot on goal

worry about whether it's going to go in or not just have to keep on

doing it and then the big idea is

where the puck is going to be

don't follow it

go to where somebody can pass you the puck that gives

you and you're you've lined up with a clean shot on the goal

so we can look

at that as a strategy and here's a

little piece of history oversimplified

but in 1968

i was in grad school i was working on this desktop

computer called the flex machine this is

a self-portrait of it on its own

screen from back then

and around

october or so september october i met

seymour pappert who was

doing computing with children

and paper and i were both mathematicians

but he had he understood something about children

that tapped into some

very aware of but i never occurred

to me that it would really work with children

i never made the connection at all i was

till on the pink plane and when i saw what paper

was doing i realized he'd come up with one of the great

ideas of the 60s maybe of the

20th century and that changed

my idea about what i was doing completely

to the point where on the plane

utah i drew this

cartoon a blue plain cartoon

of what children actually needed

and it's not so much the tablet

idea that's what people home in on

but it was the idea of taking

bart was trying to do with

human adults and

understanding what augmenting children

actually means which means

to change the quality of what's going on

their ears even as they learn these

tools so that was huge so

that was one of those kerpaus

and here's the thing you can do when you have an

idea you think is good

look around into the future to

see if there's a vehicle that's favorable

like we had moore's law

a prediction that went

out towards the end of the century

odd years so take the idea

out 30 years and look at

it out there and say

30 years from now would it be ridiculous if we

didn't have this and my answer was well yeah it would be ridiculous

moore's law says we can have it

so we should start designing it now because the design

the hard problem well the way you do that is you

this idea back to 10 or 15

years out and ask is there

something i can do here and the answer is yes

and then here's the key thing

10 to 15 years out is just

dollars away from where we are now

meaning you can

by spending a lot of money now to make

a supercomputer you can

make the computing power that's going to exist 10

or 15 years in the future as a commodity

so you spend that money that's what we did at xerox

park thanks to butler lamson

and chuck thacker especially chuck who

made this super computer

and now you've

actually invent software

rather than just piggybacking on

the software of your day you can

do many experiments and if you have a super computer

wow

you don't even have to optimize a lot of code you can do

experiments to understand

new ways of doing user interface like the one we have today

if you do optimize you can do the

kinds of applications that will exist 10 and 15

years into the future such as microsoft

word which was originally done in 1974 at

parcc and so for computing people

the simplest heuristic i can think of

is if you're trying to do

future you have to

understand

that this

as nice as it is looks sort of similar to

something that we were thinking about a long time ago

it's nice that this is this is the not

not even the present this is the past

so when i go into a research lab in a company

or i go in to graduate school i see students

to do a thesis in the future

today rather than

using machines that cost probably eighty

or ninety thousand dollars

like i see futility

it's almost impossible

progress when you're mired

in the entire infrastructure of the day

we were really lucky at xerox park

because our funders and at arpa our funders

were willing to fund

the from scratch development of both hardware and software

that is a risky business

so you have to get some chops to

do it but if you can do it and your funders will fund it

that is a way of escaping from the pink

plane okay

i'll end with dunning krueger i think everybody

knows what that means it's a

these are two psychologists who studied

uh people who were

too stupid to

know how stupid they were

uh here's a nice cartoon

this is about elitism

the passages said these smug pilots have lost

regular passengers like us who thinks i

should fly the plane and of course we have a president

he united states who thinks

the plane and the passengers

of them we'll find out

in a month or two just how this plays

out but here's the big

idea the big idea is for all levels

of ability human beings

tend to overestimate uh

uh how good they are

we all you know it's actually a

heuristic it helps to be overly

optimistic can't just

cower in a cave but in fact it's

deadly and it's something that has

to be understood and dealt with so

occasionally there are

people who undervalue themselves occasionally people are more

right on it but generally speaking

kahneman has it right

that

gener generally speaking most people are completely

unaware of how poorly they think

including people who are professional thinkers like

most of the time i'm not aware of how poorly i think

but the big difference is i know as

idea that most of my thinking must

be poor must be poorer than i

think it is most of the time

my ideas are mediocre down to bad even

one of these kerpaus so just

that as a heuristic really helps

and the other problem with being really

smart and i've known some

work with some people who are a lot smarter than i am

some of them were so smart they

had the extra 80 iq points they were

so smart that they

just

tried to bowl every problem through just from sheer

intellectual ability and lots of times they were successful

and

some of the biggest inventions though came from people who are not quite

that smart they realized

they just didn't have the intellectual capacity to deal with this

this level of complexity and so they'd

invent a new kind of programming language

that would relieve a lot of the intellectual

burden

so the point of view equals 80 iq

it could mean a minus 80 iq points

not plus it's

whatever context you choose you can choose a really terrible

context okay

let's do the q and a and

um i more or less used up my

think yeah but we started

thank you thank you alan so

we will see how many questions from the

queue we can accommodate

um i start my video thank

you so the first question is which cognitive biases

most actively working to counter

in your own life decisions

well i

the one that has always dogged

me is uh

not feeling

of my results is

o i've always been down on uh

my efforts and a heuristic

that i came up with uh that

works some of the time is whenever

feel like

i'm not doing well

enough i asked myself uh

well uh what's what's the quality of your effort

and

if the quality of my effort

if i couldn't be putting more effort in

to the thing i start feeling better

because

quality of effort is something you can control by willpower

but the complexity of the universe

means that you can't control your ideas

to be as good as

okay that really leads to

question what approaches do you recommend

prove that an abstract idea actually works

i guess that to prove something to the research community

we end up categorizing ideas like matter

rather than light well

so my research community uh

was

first it was made up of former

scientists uh in

the mathematical physical scientists sciences

and from [Music]

you know established deep engineering

so there were no undergraduate

degrees in computing

back then and this helped a lot because

all of us had been through the rigors

of dealing with highly developed fields

uh with complex

theories and complex ways of trying to

understand the theories and vet the theories and

and of course in engineering uh

one of the ways you vet things is by building models

and then you build actual bridges and

the hippocratic oath in engineering

is the the plane must not crash the bridge

nut must not fall

so the arpa and park research communities

basically

didn't spend any time arguing with anybody that

was what was nice with the funding that we had

and our view was there

that was hugely

interesting about what we were trying to do

that you could prove mathematically

although we used math in a variety of

ways and that the only way you could

vet your ideas was to actually build the artifacts

so that little

personal supercomputer the alto that we built we actually

built 2 000 of them and in today's

money they would each one of them would have been about

120 000

uh xerox uh paid for those

uh ivan sutherland did his thesis

of inventing computer graphics and

much of personal computing

in the early 60s on a

sage air defense computer that costs

uh probably 20 or 30 million dollars

and arpa gave him time on that

computer so

so in the world i came from

uh you basically built anything that

uh you uh thought was interesting

and particularly

uh for the personal computing aspect which really was

arpa was about and networking

you had to build personal computing

means user interface no matter

what else people think it is in

order and user interface is something where we do

not know enough about human beings

to be able to design abstractly and

have uh the interface

work and i can tell you that i

think it is justifiably the case

that several of us knew quite a bit more about

human beings back then

just because we had studied

them we knew

more i think than most people who do user interfaces today

but in fact we had to do hundreds of experiments

okay

thank you uh maybe we can get one more question

the answer a bit short

in order not to over stretch schedule

too much the question is is the

innovation culture quote unquote something that

engineered or is it something that

from the right incentive structure within a community

i'm particularly interested in transdisciplinary

collaboration yeah so

the first thing is uh you know we're

using these hard category words innovation

is a terrible word for what we did

at arpa and park

and this was pointed out in the 80s by regis

mckenna who was a silicon valley

figure he said apple is innovation

xerox park is invention

innovation

is complex it's difficult

it's expensive it has

things but it is uh taking an

idea and doing the packaging

it's basically incremental

to a sea of ideas that already exists

otherwise you put it trying to load too much

into innovation which is what has happened today

you're much better off saying

yeah there's this idea of invention

where even inventions come from previous

things but they're much more startling

than most of the things we call innovations

today and yes and you

can do an innovation culture

that is precisely what arpa did

and uh there's a great book

called the dream machine by mitchell raldrip which is

the history of both arpa and xerox

park it's the only really good one i know of

i've written you can find some papers

i've written about why i think the culture

worked i just did one

for the ellen macarthur

foundation over here last year which

looked at these large efforts that

required a lot of invention and had

to be done relatively rapidly by top

people with unlimited funding and i picked five

or six of them you know the radar effort

the atomic bomb effort the code breaking

effort the

sage air defense system and then i

use these as a background to look at

the principles that came out of the

park thing and you know

community and invented so many things

that it's impossible

to say well this is just a fluke

right there's actually principle

in there particularly at park where taylor

who had been an arpa funder put

into work at park what he thought

made arpa successful and he would tell you about

it if you asked him so yeah

can do it the problem is funders today

confuse being responsible

with

the feeling that they should be controlling

things and in

edge of the art research that's a disaster because

funders have not been doing edge of the art research all

their life they've been accumulating money in one

way or another they're the worst people to try and do problem

finding so every time that somebody

has tried to do a park-like place

since then some silicon valley billionaires have tried

and some seattle billionaires have tried

it's always been a disaster because

want to play and they forget

well hey you never did any of this stuff

why do you you know you don't want to

a wannabe you made billions of dollars but you just

don't have the skills to do this far

out stuff you don't know how to think about it just

put the money in and go away

and the people who can do

found and they will think of new things

that nobody else ever thought of and maybe

30 or 40 percent of them will be successful

and if they're working on a big enough problem like

we were that 30 or 40 percent that

successful will change the entire world

and in the case of arpa and park it brought

close to 50 trillion dollars of new wealth

so it's actually a good investment it's the largest return

on investment on research and history

but the funders today will

it because they can't deal

with spending five or ten years of

learning curve just to get a factor of

more money they only want millions

and billions they they can't stand the idea of trillions

so if you look at the look at the comp

anies on the uh in

the stock market that have trillion dollar evaluations

today every single one of them you

t of the technologies that were invented

by the stuff that no funder will fund today

thank you alan i think this was a very

important and very deep insight

o summarize your talk thank you very much

for the inspirational talk uh we enjoyed it very much

sorry that we can't handle more questions

i would like to invite you to join some of the other activities

the week of the heidelberg laureate forum

look into the vr space and meet some people

whatever but for the time

much for joining us and uh hope

to see you in person sometime in the

future bye-bye

uh we will now switch to the next

which is a completely recorded uh event

uh it will be given by david silver

but i shouldn't get ahead of myself because i will

introduction in this pre-recording anyway

no pause here we just continue

[Music]

stay

[Music]