# How to invent the future (part 1)

**Author:** Alan Kay
**Type:** Video
**URL:** https://www.ycombinator.com/library/77-how-to-invent-the-future-part-1
**YouTube ID:** id1WShzzMCQ

---

One of the pioneers of personal computing, Alan Kay shares his story and how to think about building for the future.

## Transcript

We have Alan Kay with us this week,
he's going to do both lectures. Alan Kay has forgotten more about how
to invent the future than progressives >> That would make a very bad class, Sam, if I have. [LAUGH]
>> [LAUGH] I think Alan is the genuine world expert on this. Invented with others, the Xerox Alto,
which we recently restored at

Y Combinator with a group of
incredible computer scientists. And I think it's the person who has been
most thoughtful, probably with anyone I've ever met, about how you build
organizations to do real innovations. So thank you very much for coming,
I am super excited to hear this. >> Great, Sam. So, I'm thoughtful about it because
I got to watch masters do it. I'm basically a research scientist, but I was interested in the process done
by far better managers than me,

who could deal with larger sets of ideas. And I'll try and give you a gist here. Basically, I think, people are here because they
want to do startups and make money. I just want to point out that
if you want to make money, don't bother with a startup. Create an industry, because then you
get trillions instead of billions. So it's about a factor of a thousand
between doing invention over innovation.

In other words, not going
incrementally from the present but carving out a whole new set of ideas
that creates an entirely new context. And we'll see some of
the ways to go about it and we'll also see some of the barriers. And see if this, no. This got a bad user interface, because it has the back button
near to the front button. See if that works, so. A lot of what these two
days are about are talking

about the place that most people
naturally live, which is the present. But the problem with the present, it is so
glittery and distracting, there's so much stuff going on. That it's hard to think about
anything except the present. And if you're thinking about the present, your ideas are going to be
derived from the present. And therefore,
they're going to be incremental. And therefore,
you wind up doing innovation, not that you can't make money that way,
but. Today, I'm going to do
the opposite of my usual order, I usually like to build
a lot of context first.

But I thought in the spirit of the Harvard
Business School and the equivalent at Stanford, I'd start off with things like
results and process and methods first. So you have a feeling that I'm actually
[COUGH] saying something that you might quote on quote apply. But the important talk
is really on Thursday, I'm still struggling with
making it the right size. So today we're going to do that, and
I urge you to copy my email address. A lot of you emails,
we're not going to have time

to have the discussion
we should have here. I welcome any questions and
by the way, while I'm talking, I welcome questions at any time,
don't be shy. Okay and here's why school pisses me off. A great man in our field, Marvin Minsky
observed that this is the best place ever to keep you from ever thinking
about anything for long enough. So you don't want to try and
learn in a classroom, it's terrible.

In fact,
I don't like to do classroom process, partly because of the time constraints. But also because it's oral, we might as well be sitting around
a campfire, a hundred thousand years ago. And almost everything that's happened
that's important in the last several thousand of years,
has been basically, literary informed. Okay, so
one of my favorite Picasso sayings, and he meant a lot of
different things by this.

Part of it is the best you can ever do
with any kind of representation is make a kind of a map, even when you're
trying to make a map of a map. You're making a lie compared to
the thing you're trying to represent. But if you do it right, people can gain some intuition
about what the map is about. That's what science is all about. This talk in 50 minutes has to be a lie,
it really is. I'm leaving out a lot of important things.

But I think the shadow of the talk or
whatever is projected by the talk is pretty close to the way things actually
are for doing this very different process. And I think Picasso didn't say,
but he knew and he meant, is art is also the lie that
tells the truth that wakes you up. So if something wakes you up in the next
two days, I will have done my job. And then, the two days are really
about another Picasso quote which is,

learn the rules like a pro so
you can break them like an artist. And not doing this is probably
the greatest sin of Silicon Valley since the 80s. Almost never, nobody has bothered becoming
a pro particularly in software and user interface design. So when they break the rules, they're breaking them like a dumb child
does by throwing rocks through windows. And it's probably the most sickening
thing to see about the field.

So another way of thinking
about the mantra is, you have to learn everything and
then find a way of forgetting it. So you can have your own ideas, but what you forget is everything
except the perfume. So when you have an idea then your
nose will pick up the right scent. And you'll be able to make use of all of
the stuff that you've learned after you've had the idea. I was specifically asked
to talk about Xerox PARC

because that was an example of making
trillions instead of billions. And, so
I thought what I'll do here is just show you a couple of results, from Xerox PARC. And I'll then try to give you some of
what it took to get those results. So, Xerox PARC is known for this machine
that happened, I gave one to Sam. He got it working with the help
of some really great people.

So this machine happened in 1973
which is 11 years before the Mac, and its screen was more than
twice the size of the Mac. It was more like a Mac of 1988 or 1989. So it was about maybe 15 or 16 years
ahead of the commercial development. And the commercial development, actually, was based on the stuff
that was done on this machine. So this is an example of the best way
to predict the future is to invent it. There's nothing like this before. Once we did it, people could see, yeah,

there could be something like
this because here it is. In fact, we made 2000 of these,
so there's a lot to look at. They have bit map screens,
they had pointing device. The famous GUI,
which you're still using today. WYSIWYG means what you
see is what you get. Desktop publishing and
the whole media gig. What does that say? That's not helping me, anybody read that?

>> Symmetrical reading and writing. >> Yeah, symmetrical reading and writing. Meaning what you almost never get
on the web, but that you did get in many of the apps of the 1980s,
which is when you get a document, the thing that you read the document with
also allows you to edit the document. So if you think about the web,
it's actually much more made for consumption than it is made for
authoring, they're completely decoupled. And most of the authoring facilities
are typing in tiny little windows, and

then pushing a button to see what you did. So this is a vast retrogression. What we call real loop these days, we just called it object
oriented programming back then. I made up that term. But what's called object
oriented programming today is not what we had back then. And I don't think I'll have time to really
talk about the profound difference. So if I have to say that what we
did at PARC became popular, and everybody wanted it even
if they only got the label.

Comparison is you can go out and buy a set
of designer jeans with the label Harvard on them, and for
all I know with Stanford on them. Laser printer,
main difference between this and what you have today is the first
one was a page a second. So most people have never printed
with a page a second printer. Postscript, outline fonts and so forth. Ethernet.

Peer-peer and client server,
and 50% of the Internet. PARC did an Internet before
there was the Internet. And we're part of that community, so
we participated in the official Internet. So we think of that as eight and
a half inventions. How long did it take? Well, 25 researchers for five years. Think about that. Two dozen people did all of these
things in about five years. Cost about 10 million to 12 million
bucks a year in today's money.

Return is about 35 trillion,
this is an old number, it's probably more like 40 now. So that's pretty good return on
investment if you think about it. If you like to do little spreadsheets and
stuff. 15% is good, right Sam? Yeah, so, and it was an industry
rather than an increment. People say, well, but
Xerox didn't benefit from this. They didn't make any money for
it, that's complete ****. It's made up by companies that
don't want to invest in research.

Xerox made about a factor
of 250 over their entire investment in PARC, so
that's 25,000% return right there. Xerox's bug was they didn't understand
the rest of this stuff, but they certainly understood what a laser printer
was, and they made billions from it. And in fact, if you look at it,
it was better for the world that they stonewalled us, because no single company can
handle an entire industry.

So this is made it possible: the Japanese
had to do printers slightly, differently than that. And this, kind of heaven on Earth,
lasted for about 12 years, Xerox finally fired the guy
who made it all happen. You're thinking,
he would have been rewarded, right, because he made all this stuff
happen, but in fact, they hated him. And they hated him for the very reason that most companies hate
people who are doing something different,

because it makes middle management and
upper management extremely uncomfortable. Last thing they want to
do is make trillions. What they want to do is make a few
millions in a comfortable way. And so this leads to
an enormous problem that where the real job of upper management in the 20
and 21st century is to learn things, because change is the constant
thing that's going on. What they tried to do is to maximize
whatever they had when they got

into the job, and
whatever the company was successful at. If you think about it,
if large companies were actually rational, there'd never be a small company. There'd be no startups, because large
companies have vastly more resources for doing new things than any
venture capitalist, right Sam? They've got gazillions of money,
but because they refuse to get into new businesses and refuse to change their
old businesses, you guys have a chance.

So, just pray that they
don't ever wake up. Now, the interesting thing is if you
look at that collection of inventions, you see every single one of them today. And what's interesting is if I were to
enlarge this a bit, I would show that there's hardly been anything interesting
invented since this funding stopped. So it's been a nuke,
basically a nuclear winter of

people cashing in on these inventions,
and extracting the wealth from them, but hardly, any efforts of any
interesting kind to go beyond them. And last point here is
the lack of curiosity. I met Sam, because he wanted to know
where'd all this stuff come from? I've hardly ever been asked that question. It's the most successful generation
of wealth in computing history,

and almost nobody wants to know, Sam did. And the difficult thing about today and
Thursday is the world that you grew up in, because I don't see anybody,
is anybody here older than 35? Okay, yeah, I see a little
more reflectivity back there. >> [LAUGH]
>> Yeah, so almost everybody in the room grew up in
a world that was unlike the world I'm going to just tell you about now.

So it's just many, many things were
qualitatively different in ways that are sometimes difficult to explain. So here's the book to read. This is why lectures suck. This is a 500 page book
done very carefully about the whole story of ARPA and
Xerox PARC. Anybody who's really interested,
read this book. And this is a tribute I
wrote to this whole research

community about I don't know 14,
15 years ago. And I'll hand it out at
the end of the class, and the main thing that is interesting
about it perhaps is the bibliography, which has a lot of references on
more detailed things you can read about how this particular
community operated, right? And the important thing about Xerox PARC,
which is not emphasized enough, is that PARC was just another one
of the ARPA research projects.

So there's eight years of
research before PARC happened. And PARC only happened
because of the Vietnam War. Nobody wanted to try to do this
stuff inside of a company. A company quarterly cycles and everything else are really
antithetical to long range thinking. So this stuff was all funded by
Cold War funds in the public domain. So none of the IP was kept secret,
but it was done in a better rhythm.

So to get the 35 trillion,
it actually required not five years, but 12 to 14 years. We were lucky researchers who
got our PhDs in this process and we're the right age to go to park and
finish it off. Right and as we'll see I'm not
going to dwell on it much more but the circa of this way of
doing things goes back, especially to the radar effort at MIT and

the air defense effort and
then upper and the park. So there is a long continuity
here of kind of how do you, work on things that are,
That are doable but where you have to invent several generations of technology
to get to the thing that's doable. So most of these things are not doable
with the technology that's lying around. That is the problem with
these hard problems.

Okay, so the general world,
the normal world. The present, for most of this period, was either punch card accounting machines,
or their replacement. After IBM said famously they'll no,
there's no room for more than five or six computers in the entire world, they wound up doing the first
mass produced computer, the 1401. The first computer I ever programmed. To replace their punch card machines
before other computer companies did.

So they did a sort of Trump like reversal,
on their belief and the bound up owning the 60s and
much of the 70s. And most important thing,
this is a dumb sentence because, you don't know what these
machines were like. So I realized after I put it in there
that, why did I even put this in, right? But the way I look at what's
going on at any given time,

whether it's today, 30 or 40 years ago. Is whatever's going on right now
is just crap, by definition. If we know about it,
except in the 1/10 of 1% or 1000 of 1%, it's gotten mundane. And part of it is just because of
the bell curve of normality in humans. Whatever it is, it gets converted
to something like normal.

No matter how exciting it is. And so when things are widely successful
they tend to bring up the mean of the bell curve a little bit,
for everybody, raises all boats. But in fact, there's also this regression
to the mean on almost all of these things. So living in the present, man, you're just out of it if you're trying to
think about things from what we have now. Now there are two processes. There's the bomb project and
the radar project at MIT,

that had roughly the same process,
roughly the same difficulty. You have to realize the US was in
World War II for only about two and a half years. Pearl Harbour was December of 1941 and so we had 42, 43, 44,
three and a half years. And a lot of things got done
the Most interesting thing is for the first time in history, really,
a lot of really good scientists and

a lot of really good engineers started
working together and cloning each other. So seven Nobel Prizes came
out of the building 20. Because they were physicists who
put on their engineering hats. To make 185 different
kinds of radar systems and install them in every size of building and
plane and boat. And World War II was
basically a war of supply. And it was the ability to a Stave

off the German submarines that
had actually won the war for us. Most people don't think of it that way. But that's what happened. So in the circa I'm talking about
I came out of this group and there's a couple of good books about how
these people went about doing things. Maybe the number one thing is what I have
on right hand side is basically he said, forget about your ego, I really meant it. It doesn't matter who you are,
how smart you are, how smart you think you are,
there's only one thing that counts here,

is making progress and
we make progress through synergy and they learned how to do this and they
passed it on generation, after generation. Well the next round of this,
after World War II, was the cold war. And the air defense system
that was done in the 50s. And again at MIT, the first displays
that you could interact with. That is essentially a stylus in the guy's
hand, it was called a light gun.

So he's pointing at something on
the screen and squeezing the trigger. Like you would put a Silas down and
push it down and the light gun can tell, computer can
tell what the light gun is working at. So you can do all of the stuff,
that you're used to today. To give you an idea of
what these guys did, I can't really see what this is right? It's just like it's obviously
four floors of a building. Now, this is a football field.

And if you notice the second floor,
it says computer A and computer B. Each one of those computers
had 50,000 vacuum tubes. Both running the same programs
at the same time and many other interesting things I don't have time
to talk about but, I'll just say that when one of these computers started crashing
it took it three or four days to crash. And the reason is,
it was running diagnostics on itself. And every time an instruction failed,
it would patch in a simulated instruction based on
what instructions were still working.

So what would happen is the machine
would just get slower and slower and more software-like. More like a Turing machine and
usually they could fix it before it came all the way down,
meanwhile the other one was still working. But, even though I
shouldn't be digressing, there's a fun thing here, there were
32 of these concrete bunkers made. So the two interesting things,
what happened to this stuff, anybody know? Does this look like anything
you've ever seen before?

>> Space program stuff? >> No, that's, but-
>> Airline meter, sorry. >> Yeah, yeah,
this actually was the invention of our, air traffic control system. That's what it was designed to do,
except that it was designed to control traffic of both American and
Russian bombers and in fact, if many of the displays before
they replace them with flat screen. Displays is basically the same big round.

So this whole system last until 1982. When the last one was finally
decommissioned and 50,000 vacuum tubes. They're like incandescent light bulbs. They blow out, so
they're always blowing out. So, of course,
there are redundant ones there. Where did we get the vacuum tubes from? Think about it,
all the way through the 70s. >> [INAUDIBLE]
>> [INAUDIBLE]

>> No, this is back, no transistors in these machines. No transistors, these are-
>> Russia. >> Absolutely. How did you know that? I heard it before. >> Yeah. >> [LAUGH]
>> That's good, and you remember it. That's good, yeah? >> For the last 12 or
18 years of this defense system, which was never used against the Russians
ever, because they never tried to bomb us. And was actually obsolete very soon
because of ICBMs, it couldn't track them.

There's a whole other system for
doing that, yeah. But we kept it going and
there are reasons why it was kept going. We bought while we're still
contending in the Russia for the cold war,
we buying vacuum tubes from them too. By the way, people still keep buying
vacuum tubes from the Russians for Getting old 50s guitar amp sounds. Those overdriven sounds. And this guy, who was one of the inventors
of artificial intelligence, and

the inventor of the programming language
LISP, John McCarthy, looked at one of these in the 50s and said, Everybody is
going to have one in their home someday. Because he didn't give a **** about the concrete bunkers or
anything else like that. Because what he thought was, yeah, this is
like a electric power generating station. Nobody ever sees them but
they're out there. We have wires going to the home for,

it's like where we get our water from,
it's where we get our gas from. The utilities, so he thought there
would be an information utility, and it will actually be a human right,
like the telephone, to have one of these things In your home that is
connected to all the worlds information. So that was one of the earliest and
most influential ideas. 1962, I'm going to show you a system
done on one of these super computers.

This is done on the test computer at
Lincoln Labs for this whole SAGE system so this computer was close to
the size of this entire building. With one guy on it,
yeah at 3 o'clock in the morning. So, take a look at this. This is Ivan Sutherland. So, it doesn't really even have a display. It's actually simulating
a computer display here. This is just an oscilloscope.

So, what Ivan wants to do,
is to draw a flange and so he says, it's kind of like this. Now take these guys and
make them all mutually perpendicular and wow, sketch pad just solved that problem. So it's a dynamic problem solver in there. First window then clipped. Now it wants to put a hole in the flange. So these are guidelines. and the first thing he does is said,
okay, I want to make this parallel. And you see, sketch pad keeps them
on the line there and lines them up.

And now, he's using them as
guidelines to draw a dash lines. You see here, he misses Whoop, okay. Okay, and
now he makes the guidelines invisible. They're still there. The constraint was co-linearity there. And he has a knob to continuously zoom.

So this is the first
computer graphics ever. And he wants some rivets to go along
with that flange, and so again he, this is why this system is called a sketch
pad because you just casually draw. Just going to use that as the center for
the ark here. And again he's going to say,
take these guys and make them mutually perpendicular and
here sketch pad solves that problem.

So you wind up with a symmetric object. And he can change things and he'll get another solution. He could have constrained the side
links to be ratios of each other. And the kind of problem
solving this system could do, well included non linear problems. So there, he's got a rivet.

And what's cool about this,
that is a master rivet, what we'd call a class in
object oriented programming. So this is not that rivet, but
an instance of that master rivet. Might wonder, why is that display
bouncing around like that. >> Well it's putting up
every dot individually, at about half the power of this super
computer is being used to just do that. So here another instance, another rivet.

Here is another one, here's another one. And he says whoops I didn't want
to have those crossbars there, so I'll go back to the master rivet and
make the crossbars invisible. They're still there but invisible,
and we see the instances. So this is object oriented programming. Maybe nicer than you've seen it. Get rid of those guys and now, that construction that he made,
he's made it into a master.

So he can make instances of it. Okay, get the idea? >> I had a question. >> Yes.
>> [INAUDIBLE] Sort of regressed from here
>> Well anybody in this class ever seen SketchPad before? Okay, so that's part of the answer. Yeah we'll go along, it's sort of
the larger question that we have.

It's worthwhile bringing up the question
He's rotating three of them. So, this is the most shocking thing
I;d ever seen when I went to graduate school in 66. This was, the system was only
three years old at that time. And I've been programming for
five years and just for conventional programming and
seeing this, it blew my mind. Because it was exactly different than
everything I thought about computing.

As soon as I saw I, I realized yeah,
of course you can do that. But I didn't think about that. Ivan did. Okay so Sketchpad, interactive computer
graphics in a way we recognize today. For the first time, objects,
masters and instances. The programming was not done by
the kind of programming today, but by problem solving, which I think
you can imagine is much nicer.

Like it will find the solution. And it creates automatic
dynamics simulations, so it's not just for drawing bridges. When you draw the bridge in,
it knows how to simulate the bridge and tell you what the stresses
in this trains are. So I said to Ivan, Ivan you did all
of this and what is this PhD thesis? Said, you did all this in one year by
yourself, how could you possibly do it? And he said, well,
I didn't know it was hard. >> [LAUGH]
>> He just went after what the problem is.

And if you read his thesis,
and you should, because you can see there are things that
are of absolute goodness still today. It's not just relatively good for
being done more than 50 years, it's absolutely good. And his thesis is, every other page is
an apology because it doesn't do more. because Ivan was working on the problem. He wasn't working out what you could do,
he was working on the problem. Yeah, so sketch pad was a bombshell in this research community
that was about to happen.

because right away,
you were looking at the future. You just had to believe that
a building sized computer was going to wind up on a laptop, or
even something in a desk. So the main player here back then
was a guy by the name of Lick. Licklider, he got given some money
in 1962 by ARPA before the day, and when anybody asked him what are you
going to do, this is what he would say.

Computers are destined to become
interactive intellectual amplifiers for everyone in the world,
universally networked worldwide. He would not say anything more. Simply gave out money. Now here's some bullet points. I hate bullet points, but this is a perfect class I
think to put bullet points in. And I found 16, that will tell
you just what you have to do. And I've thought of a few since,
but 16 is more than enough.

So the first thing, was just picking
an idea that's worth dedicating your life, if necessary to. So, this stuff was human destiny, fixing big human problems,
like we can't think very well. We need to make things
to help us to think, we need to make things
to help us cooperate. So these were save the world kind of ideas
and they were done when the Russians where starting to test hydrogen bombs and
things did not look so good.

Forget about goals, the problem is that goals tend to be much
more idiosyncratic to individual humans. So research wants to be a vision. So notice there aren't any
goals in the ARPA dream. And that allowed Licklider to fund 15 or
20 super smart people who thought they had
ways of approaching the dream. And some of these people didn't
[BLANK AUDIO] agree, and some of them hated each other.

And Lick didn't give a ****, he just
wanted smart people working on this dream. So fund people, not projects. ARPA never decided. And we'll see a slight
modification of this. But basically, fund people, not projects. If you're going to do that,
you better have the very best people. So, if you know,
MacArthur grants are for individuals. But this funding was funding groups.

Like you fund in MacArthur,
just five years, forget it. Nobody at MacArthur asks,
you don't get a second MacArthur grant. Here, they would get another grant if
they'd done something good in five years, but basically the idea of
MacArthur is throw away. We've identified this person of extreme
potential, let's just give him five years of funding and
we won't cry if they don't do anything. It turns out most MacArthur people
do something because the people that attract attention are people
who are not working for money.

They're doing it because they must, they are people like artists are people
who do their art because they must. Community not a project,
have to fund problem finding, this really drives funders crazy today. What do I mean by that? Most of the time,
when you are working on hard problems, you don't know what the right problem is. This is why visions are really good. Visions are detached. If you pick a problem too early you might
be picking it out of the current context.

And therefore, you're going to be
hampered unless you are incredibly lucky. So ARPA put a lot of money into just
people thinking around with stuff. Milestones not deadlines. Baseball not golf. Meaning, when you lose a stroke in golf,
you cry. When, you strike out in baseball, you
better not cry, because you're going to do it a lot, and
this is what Licklider said to them. He said look, if you're batting 3.50
in baseball, you're really doing well.

And if you look at what we're
funding if we bat 3.50, we're going to change the world. That's what happened. Nobody cares about all
the stuff that didn't work. And people said,
well what about the 65% failure? And they said, well it's not
failure in baseball, it's overhead. Hitting a ball is hard, when you're doing
something really, really hard, the times you don't do it well is just overhead for
doing it the times you do well. And this is probably the biggest
distinction that business people do

not understand. because what they want is actually teeny, little uninteresting projects that
are guaranteed for your success. But sports is right in front of it. Sports is really hard, and most sports
people are not succeeding all the time. Anybody know baseball here? What's the thing in baseball,
it's called an error? Like what? >> [INAUDIBLE]
>> No, just fielding. >> Error.

>> Yeah, what's an error in baseball? Not catching a fly ball. How good are the average fielders? They're 98.5% effective. So, really good ones are like one
percent error and so an error and technical stuff is designed to build
a computer system and failing to build it. Like anybody should be, decide to build
a software and failing to build it. You just should be able to knock that off. But you're in this other range
when you're trying to do design.

And it's really two different things. So, here's a memo Lick wrote in 63, shortly after he got this initial
money from ARPA to members and affiliates of
the Intergalactic Computing Network. And they asked him,
why did you call it that? He said, well engineers always give you
the minimum, and I want a network that spans the entire planet, so
I'm asking for an intergalactic one. And when they scale it down,
we'll still get, so

that's where the internet came from,
literally. The original name of the Internet
was the intergalactic computing, nobody knew how to do it back then. For instance, packet switching
had not been invented in 63. And here's a nice line in that memo,
if we succeed in making an intergalactic network, then our our main problem will
be learning to communicate with aliens. And he meant this in
the biggest possible way, and I don't have time to really explain it,
it's really interesting. People who are interested in
this should write me an email.

He didn't mean just other people. He meant other software, other computers. He meant what does it mean to
communicate when you scale things up? So this guy was a big thinker. Number nine,
you can't think inside the Beltway. That's of course referring to Washington,
DC. But this is a general principle. They asked him why, and he said,
well, because there's too much noise. There's just too much politics. There's too much ****. And nobody does research in Washington,
DC. So the last thing we want to do,
as our profounders, is to try and

think while we're there. Our job is to get money out of
the government and pass it along. And so a solution to that would say,
hey let's not be here for longer than two years. And so every two years, so Lick set
up the process to get his successor, happened that Ivan Sutherland got drafted
into the army at just the right time. And so they grabbed him and so at age 26 Ivan ran this whole show and
man was he good.

He was a second lieutenant sharing
meetings with generals and one of the most famous
things recalled of that. Some general was going on and
on at some point Ivan said, general you have just two minutes
to make your point if you have one. That's about the simplest
way of describing Ivan. Bob Taylor and Larry Roberts. Those are the four that made this happen. Taylor is special because he is
also the guy who set up park.

And he was a student of Licklider. Licklider was intuitively wonderful, Taylor was a student of what
was wonderful about Licklider. And he could explain everything that
Licklider could do and why it worked. So here's a couple things,
I'm not going to go about, but basically the idea here is it
isn't like lets look around and see what is available and
what we can do with it. The idea was stick with the vision and just make every frigging
thing that's necessary.

It doesn't matter what it is. If we have to make a new kind of
integrated circuit, we'll do it. All of these things were done. So it's very much like these other
cultures where nobody worried about whether you had half centimeter radar in
building 20 at MIT, they just did it. And here's one that is really a bug today. And if you don't have the chops,
yeah you shouldn't make your tools, you shouldn't make your
own operating system. You shouldn't make your own programming
language because that's not what you're

trying to do. If you do have the chops, and you better
not do his unless you have the chops, then you have to make your
own hardware and software and operating system in
the programming languages. Otherwise you're working in the past
on some vendor's bad idea of what computing is about. So part of this deal,
remember what Picasso said. You have to get really much,
much better than what most people want to today,
and here's another reversal. Today people buy hardware and

put software on it basically to
make the hardware look good. The ARPA community in part
did exactly the opposite. It started off with the software. Using super computers
to simulate the thing. And when you got the software
the way you wanted it, then you'd design the computer
that would optimize and make more efficient what you
were doing on a super computer. That is what Sketchpad was. Nobody thought that the next graphic
systems were going to be done on a computer the size of this building.

Okay, and then make a bunch of them. So almost every project
in the ARPA project, they actually made enough of them so
they could be used as tools. They weren't just demos. And so part of this invention process had
to require a kind of limited engineering. Park, for instance, had a thing where whatever
you did you had to make 100 of them. Made an Ethernet,
it had to run 100 machines. If you made a time sharing system,
it had run 100 users. If you made a personal computer,
you had to be able to build 100 of them.

Learn how to argue. This is what you learned as
a graduate student there. Argue for clarity, not to win. It's the biggest bug today. People are always contending with each
other, trying to be winners and losers, and that's one of
the problems with Washington, they've forgotten what their job is. Now what you have to do is
understand these complicated things. Here's a biggie,
every researcher at Park was a second or third generation PhD
that ARPA had created.

Right, eight years. It wasn't just the stuff in the past. I'll show you a couple more of those,
wow we're getting closed to, but it was creating the next generation. Again, this is baseball. Baseball you have to develop talent going
all the way the down to little league. And they did and
the other thing is a little difficult to, some of you will understand this readily. That the reward of doing this stuff
wasn't the reward of making it happen

because a lot of times it didn't happen. It was a reward of actually being funded
to work on what the actual problems were. I can't emphasize this too much. Working on what the problems actually are
rather than something that's going to get a paper, something that's going to make
you money, but taking big human problems. Could be something like drinkable water. For the 70% of the planet
that doesn't have it.

Doesn't matter, there's no other goal. If you pick one of those things that's
a great one, worth putting your life into. Okay, so background was partly tinkering. A lot of people came from New York,
down where the world trade center was. Before the world trade center, there was
about a mile across Manhattan Island that was nothing but electronic surplus stores. Mow a few lawns,
put a dime into the subway and

you could go down there and
buy almost anything to mess around with. And that group got used to,
everybody was broke. There was a kit to build
your own oscilloscope. And if you wanted an oscilloscope and
you were broke, you could get one of these on time for
$30 or $40 bucks and build it. And I'm going to just

put, these are just washed out anyway so
I'm just going to go past. Okay, so Moore's Law, this was
the original thing in Moore's paper. Doubling every year. He picked MOS silicon which is too
slow to make things out of, but would get faster if you made it smaller. Here's doubling every two years,
and what happened. The prediction was 30 years and so
what happened was, very in line

with doubling every two years to every 18
months, and there is physics behind this. This wasn't just an engineering
aspiration, and so if you believe this you had
something really worthwhile. And I'm going to skip past Engelbart here. >> Set it up so I see it like that,
that leaves a corner. >> I think you should see
a little of this though, because the same time the mouse was
invented this was done at Rand. And how did the Rand people go about it, well at midnight they will go through
people's waste paper baskets.

To see how they worked,
what were they throwing away? And what people were doing when
they were working was making all kinds of diagrams and
little flowcharts and all this stuff. So they said, okay,
well let's invent the first tablet, As good as most of the tablets
you've ever used today. It's the hallmark of these people is they
generally did it good enough and here's- >> You may start to edit the flow diagram. First we erase the flow arrow,
then move the connector out of the way, so

that we may draw a box in it's place. The printing in the box is being used
as commentary only in this case. The box is slightly too large,
so we may change its size. Then, draw a flow from
the connector to the box. Attach a decision element to the box,
and draw a flow from it to scan.

We then erase the flow-
>> Okay so this is about 1968 or so. Again on a big room sized mainframe,
with one guy. But, this system really, you could ask
your question even more about this. This system was [LAUGH] one of the best
systems I've ever used in every. It felt so intimate, it was so
different from the mouse. It was one of the things
that we actually looked at.

I guess I do have to
show the next thing here. Just so you think that VR
wasn't something done recently. But the second thing Ivan
did after he came back, the thing that when it came
back from Arpo was to do these. I worked on this one when
I was a graduate student. You could grab things and have
the thing in your hand, grab things and move them around it. It's a little exciting because instead
of the thing that you used to today. In the art had two CRTs with 15,000 volts
right above your ears crackling away.

So it was a very exciting thing to do and,
of course, one of the hardest things was to do
good head positioning back then. There are many ways of doing it. One of the things they did here,
I won't explain what it is, but it was hooked to a crane. So as you walked around
this big room at MIT, a crane would automatically follow you
with the positioning thing over your head. To find out what this was about. And, man, I'm getting killed
because I should stop right now.

But I really have two more things to do,
if you could give me two more minutes, I will do them. First one here is,
this is something you have to think about. Let time go one way, and
progress go the other way. Yay boo, yay boo, it goes up it goes down. This is the way people
tend to measure things. The problem is they never
put in a threshold. If you put in a threshold, then the only
things above the threshold count. Like if these are reading scores,
Nothing counts.

We, of course,
never get above the threshold. So it doesn't matter whether they go up or
down. And, what is actually needed
changes over in time. You need more, and if you're measuring
to a baseline, which people usually do. One of the ways of improving things, or making it look like you're not doing such
a bad job is to lower the base line. For example, Apple completely
lowered the base line on what constitutes reasonable user interface for
iPhones and iPads.

Interfaces on the system beforehand
had an undo, and these don't. And I can name 15 more things. Think about it. So what they did is they decided, well we're just not going to work
on all of those problems anymore. We're going to condition
the unsophisticated public to do work at the level of a two year old,
or a 92 year old. And we're just going to
eliminate everything in between. And the public has bought it, because you don't want to count noses
when you're looking for quality.

People can be talked into anything. So what you have to do on this
stuff is you have to pick something that is
absolutely above that line. We call that MacCready "Sweet Spot",
he's the guy who did manpowered flight. And once you have achieved that,
it opens up a whole region that you can explore, and
that's what we did at park. At Moon Shot,
was set space travel back 50 years. Everybody uses a metaphor
we need a moon shot.

No we don't need a moon shot. You just don't do space travel
with chemical rocketry. And what’s interesting about
the people who like Jeff Besolson. Yeah, Elan, [LAUGH] they don't get it. Mv = mv. Every child who read science
fiction in the 50s knew this. What that means is, you either have to
carry a shitload of reaction mass with

you, if you're doing chemicals, because
you can't get the velocity high enough. So you have to put out a lot of mass, and
if you do that you have to lift that mass. So you wind up with 45 story building
rockets just to get into orbit. That is nuts. Anyway, I will not go on that. So, but the thing that was a tragedy was
that they were very good proposals for how to get that high exhaust velocity
Using various forms of atomic power.

And it was something that
the public was not interested in, the moon shot was not about space travel. Okay, so, I'll skip past this. Because I want to end with,
yeah, here's, so this tablet computer I thought up in 1968. It had two initial forms. One was the familiar tablet, and the other one was what Ivan's had mount of
display was inevitable with Moore's Law. And then, Nicholas Negroponte had
this idea of wearing a watch and

communicating with the rest of the world. Okay, so here's the last little segment,
and then I'll let you go. Wayne Gretzky,
you know who Wayne Gretzky, is I'll bet. Greatest hockey player who ever lived. And he was just a little guy,
he tried to avoid fights. They asked him why he took so
many shots on goal. And he says, well you miss 100%
of the shots you don't take. So he wasn't trying to be careful.

He scored more goals than anybody
in history by a thousand. So, the fact that his percentage of misses was also high was irrelevant. And they asked him,
why he was better than anybody else? And he said, well, a good hockey
player goes to where the puck is, a great one goes to where
the puck is going to be. And he didn't mean tracking the puck. He meant getting into a place where
somebody could pass him the puck where he could make a goal. So what he did is he looked
at the entire configuration,

saw where the future was going to be,
and went to that place in the. So you can make a game to
invent the future out of this. And so you start off with
a cosmic goodness intuition. Like for me that tablet one was good. You identify a favorable exponential,
like Moore's Law. You take the cosmic
intuition out 30 years, and you ask, can we say, wouldn't it
be ridiculous if we didn't have this. And say 30 year out, or 30 years away,
well of course, we'll have one.

That's what that exponential means. And bring it back to the 10,
15 year point. And that point, you can just pay money
because that's also what Moore's law and what Turing means. Is, if you pay a lot of money now, you can make the commodity computer of 10,
15 years in the future. That's what the Alta was. It was about 50 times faster than what
you got out of the time sharing terminal. And make a bunch of them, And
you intertwine it, so, run the software.

And then you can do two kinds
of computing in the future. One kind of computing is zillions of
experiments to get a user interface that would be universal for. Right now, 5 billion people, and deal with millions of people who were doing
applications you've never seen before. And the other thing you can do, the thing on the right there is Microsoft
Word as it was at Xerox Park in 1974. If you optimize the code, you can get what the applications
are going to be ten years out.

So those are the two things you can do
by doing this super computer thing. And it cost money. In today's dollars those altas
cost about 125K a piece, and we made two thousand of them. Think about that. Got to be a funder who's serious. Xerox went bat **** when we did it. They really went bat **** when
we wanted to cash them in. But I'll just leave you this
since I'm over time now. I'll leave you this as one of
the ways of escaping the present.

Have a glimmer of an idea, take it so far
out that you don't have to worry about how you're going to get there, and
then you just bring it back. So instead of innovating
out from the present, what you want to do is to invent
the future from the future. You are living the future,
and bring the future back. Thank you.
>> [APPLAUSE]
