How to Invent the Future I - CS183F
From Viewpoints Intelligent Archive
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,
[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
ver met, about how you build organizations to do real innovations.
So thank you very much for coming, I am super excited to hear this.
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
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, 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
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,
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
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.
we just called it object oriented programming back then.
I made up that term.
But what's called object oriented programming today is
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
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.
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?
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,
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.
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
If you think about it, if large companies were actually rational,
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,
And what's interesting is if I were to enlarge this a bit, I would show that
here'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.
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.
Nobody wanted to try to do this stuff inside of a company.
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,
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
he 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.
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.
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
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,
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.
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
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?
>> 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 transistors in these machines.
No transistors, these are- >> Russia.
I heard it before.
>> [LAUGH] >> That's good, and you remember it.
>> 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
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.
So, what Ivan wants to do, is to draw a flange and so he says,
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.
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.
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.
>> 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.
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
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
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.
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,
When you draw the bridge in, it knows how to simulate the bridge and
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.
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,
And his thesis is, every other page is an apology because it doesn't do more.
He wasn't working out what you could do, he was working on the problem.
Yeah, so sketch pad was a bombshell in
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.
Simply gave out money.
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.
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.
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.
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
tract attention are people who are not working for money.
they are people like artists are people who do their art because they must.
Community not a project, have to fund problem finding,
Most of the time, when you are working on hard problems,
you don't know what the right problem is.
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.
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,
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
because what they want is actually teeny,
little uninteresting projects that are guaranteed for your success.
Sports is really hard, and most sports people are not succeeding all the time.
What's the thing in baseball, it's called an error?
>> [INAUDIBLE] >> No, just fielding.
>> 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.
But you're in this other range when you're trying to do design.
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.
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 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.
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.
And nobody does research in Washington, DC.
So the last thing we want to do, as our profounders, is to try and
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
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.
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.
Taylor is special because he is also the guy who set up park.
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.
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
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
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.
Using super computers to simulate the thing.
then you'd design the computer that would optimize and
That is what Sketchpad was.
Nobody thought that the next graphic systems were going to be done on
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.
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.
Argue for clarity, not to win.
People are always contending with each other, trying to be winners and losers,
and that's one of the problems with Washington,
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.
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.
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
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.
>> 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.
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,
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.
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.
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.
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.
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.
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.
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.
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
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
Is, if you pay a lot of money now,
you can make the commodity computer of 10, 15 years in the future.
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.
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.
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]