How to invent the future (part 1)

the rest of us. Would make a very bad class, Sam. But 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 he's the person who has been most thoughtful, probably with anyone I've ever met, about how you build organizations to do do real innovation. So thank you very much for coming. I am super excited to hear this.

Great, Sam. So,.

well 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 because people are here because they wanna do startups and make money.

I just wanna point out that if you wanna 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. See if this, no, this has 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 gonna be derived from the present. And therefore, they're gonna be incremental and therefore, you wind up doing innovation. Not that you can't make money that way.

But today, I'm gonna 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 saying something that you might quote unquote apply.

But the important talk is really on Thursday, I'm still struggling with making it the right size. So today we're gonna do that and I urge you to copy my email address. I love emails. We're not gonna 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. 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 wanna 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 100,000 ago. And almost everything that's happened that's important in the last several thousands of years has been basically literary in form. Okay, so one of my favorite Picasso sayings, 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 fifty 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 a thing that 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, 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.

And 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 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 eleven years before the Mac and its screen was more than twice the size of the Mac. And it was more like a Mac of 1988 or 1989.

So it was about maybe fifteen or sixteen 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 was 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 2,000 of these. So there's a lot to look at. They had bitmap 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? It'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 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. 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 differences. Suffice to say that what we did at Park 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. Post script, outline fonts and so forth. The Ethernet, peer to peer and client server, and 50% of the Internet parked at 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 10,000,000 to $12,000,000 a year in today's money. Return is about 35,000,000,000,000.

This is an old number, it's probably more like 40. Now, that's pretty good return on investment if you think about it. 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 bullshit.

It's made up by companies that don't wanna invest in research. Xerox made about a factor of two fifty over their entire investment in Park. So that's 25000% 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 than they Stonewalled us. Because no single company can handle an entire industry. So this made it possible, the Japanese had to do printers slightly differently than that. And this kind of heaven on earth lasted for about twelve 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 them for the very reason that most companies hate people who are doing something different. Because it makes middle management and upper management extremely uncomfortable. The last thing they wanna do is make trillions. What they wanna 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 twenty and twenty first century is to learn things. Because change is the constant thing that's going on. What they try to do is to maximize whatever they had when they got into the job and whatever the company was successful at.

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? You'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, 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 basically 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 the last point here is the lack of curiosity. Sam is a huge, I met Sam because he wanted to know where did 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.

Yeah, so almost everybody in the room grew up in a world that was unlike the world I'm gonna 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. This is a tribute I wrote to this whole research community about, I don't know, fourteen, fifteen years ago. And I'll hand it out at the end of the class. And main thing that's 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, that PARC was just another one of the ARPA research projects. So, there's eight years of research before Park happened. And Park only happened because of the Vietnam War. Nobody wanted to try to do this stuff inside of a company.

The 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 35,000,000,000,000, it actually required not five years, but twelve to fourteen years.

We were the lucky researchers who got our PhDs in this process and were the right age to go to Park and finish it off. Right, and as we'll see, I'm not gonna dwell on it much more, but the zeitgeist of this way of doing things goes back to the, especially the radar effort at MIT. And the air defense effort, and ARPA and then Park.

So there's a long continuity here of kind of how do you work on things 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, 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 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 a Trump like reversal on their belief. And wound up owning the 60s and much of the 70s. And most important thing, 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 sentence in?

Right, but the way I look at what's going on at any given time, whether it's today, or forty years ago is whatever's going on right now is just crap. By definition, if we know about it except in the one tenth of 1% or one thousandth 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 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 Harbor was December of nineteen forty one, and so we had forty two, forty three, forty four, 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 thing 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 stave off the German submarines that actually won the war for us.

Most people don't think of it that way, but that's what happened. So, and the zeitgeist I'm talking about 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 the right hand side is basically they said forget about your egos and 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 the light gun. So he's pointing at something on the screen and squeezing the trigger. Like you would put a stylus down and push it down and the light gun can tell, computer can tell what the light gun is looking at.

And so you can do all of the stuff that you're used to today. To give you an idea of what these guys did, You can't really see what this is, right? It's just like, it's obviously four floors of a building. This is a football field and if you notice the Second Floor there 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. 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. 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 are 32 of these concrete bunkers made. So the two interesting things, what happened to this stuff?

Anybody know? 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 it was designed to control traffic of both American and Russian bombers.

And in fact, if many of the displays before they replaced them with flat screen displays with Basically the same big round things. So this whole system lasted until 1982. When the last one was finally decommissioned and 50,000 vacuum tubes, like incandescent light bulbs. They blow out, so they're always blowing out. So of course there are redundant ones there. Where do we get the vacuum tubes from?

Think about it, all the way through the 70s. No, no this is vacuum, no transistors in these machines. No transistors, these are the.

From Russia. Absolutely.

How did you know that?

I've heard it before.

Yeah. Well, that's good and you remembered it. That's good, yeah. For the last twelve or eighteen years of this defense system, which was never used against the Russians ever because they never tried to bomb us. It was actually obsolete very soon because of ICBMs, it couldn't track them. There's a whole another system for doing that, yeah.

But we kept it going and there were reasons why it was kept going. We bought, while we're still contending in the Russian for the we're buying vacuum tubes from them too. By the way, people still buy vacuum tubes from the Russians for getting old 50s guitar amp sounds. Those over driven 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's gonna have one in their home someday. Because he didn't give a shit about the concrete bunkers and anything else like that. Because what he thought was, yeah, this is like an electric power generating station.

Nobody ever sees them, but they're out there. We got wires going into the home for it. It's like where we get our water from, it's where we get our gas from. So utilities, so he thought there will 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 world's information.

So that was one of the earliest and most influential ideas. 1962, I'm gonna 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. This computer was close to the size of this entire building, with one guy on it at 03:00 in the morning. So take a look at this. This is Ivan Sutherland.

So it doesn't even really 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, okay, it's kinda like this. Now take these guys and make them all mutually perpendicular and wow, Sketchpad just solved that problem. So it's a dynamic problem solver in there.

First window that clipped, now he wants to put a hole in the flange. So these are guidelines and the first thing he does is said, okay, I wanna make these parallel. And see, Sketchpad keeps them on the line there and lines them up. And now he's using them as guidelines to draw dashed lines. You'll see here he misses, whoop, okay. Okay, and now he makes the guidelines invisible, they're still there.

The constraint was called 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, this is why this system is called sketch pad because you just casually draw. He's gonna use that as the center for the arc here.

And again, he's gonna 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 lengths to be ratios of each other. And the kind of problem solving this system could do were included non linear problems.

So there he's got a rivet and what's cool about this, that is a master rivet, what we call a class in object oriented programming. So this is not that rivet, but an instance of that master rivet. You might wonder why is the display bouncing around like that? Well, it's putting up every dot individually and about half the power of this supercomputer is being used to just do that.

So here's another instance of the rivet, here's 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 and so he can make instances of it. Okay, get the idea? Alan, I have a question. Yes. What has gone wrong to have sort of regressed.

here?

Well, anybody in this class ever seen Sketchpad before? Okay, so that's part of the answer. Yeah, we'll pick that, go along. It's sort of the larger question that we have to, it's worthwhile bringing up the question, if he's rotating three of them. So this is the most shocking thing I'd ever seen when I went to graduate school in 1966. This system was only three years old at that time.

And I've been programming for five years and just 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 it, I realized, yeah, of course you can do that. But I didn't think about that, Ivan did.

Okay, 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. It will find a 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 and strains are. So I said to Ivan, Ivan you did all of this, this is his PhD thesis. He said, you did all this in one year by yourself, how could you possibly do it? He said, well I didn't know it was hard.

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 fifty 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 on what you could do, was working on the problem. Yeah, so Sketchpad was a bombshell in this research community it was about to happen. Because right away you were looking at the future. You just had to believe that a room, a building sized computer was going to wind up on a laptop or even something at a desk.

So the other, 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 D. And when anybody asked him what are you gonna 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 were starting to test hydrogen bombs and things did not look so good. Forget about goals.

The problem is the 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 agree and some of them hated each other. And Look didn't give a shit.

He just wanted smart people working on this dream. So fun people not projects. ARPA never decided, and we'll see a slight modification of this. But basically, fund people not projects. If you're 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 funded McArthur. Just five years, forget it.

Nobody at McArthur asks, you don't get a second McArthur 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 them five years of funding and we won't cry if they don't do anything.

Turns out most MacArthur people do do something because the people that attract attention are people who are not working for money. They're doing it because they must. They're people like artists are people who do their art because they must. Yeah, not a project. You have to fund problem finding. This really drives funders crazy today. What do I mean by that?

Most of the time when you're 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 gonna be hampered unless you're incredibly lucky. So ARPA put a lot of money into just people dicking 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 gonna do it a lot. And this is what Licklider said to them. He said, look, if you're batting three fifty in baseball, you're really doing well. And if you look at what we're funding, we bat three fifty, we're gonna 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, it's not failure in baseball, it's overhead. Hitting a ball is hard, and when you're doing something really, really hard, the times you don't do it well is just overhead for doing it at times you do well.

And this is probably the biggest distinction that business people do not understand. Is what they want is actually teeny little uninteresting projects that are guaranteed for success. But sports is right in front of us. Sports is really hard and most sports people are not succeeding all the time. What's the thing in, anybody know baseball here? What's the thing in baseball that's called an error?

Like what? 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 1% error. So an error in technical stuff is deciding to build a computer system and failing to build it. Like anybody should be able to, or deciding to build a software system 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? And 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. Packet, instance, packet switching had not been invented in '63.

And here's a nice line in that memo, if we succeed in making intergalactic network then 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. 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. And they asked him why and he said, well because there's too much noise, there's too much politics, there's too much bullshit, and nobody does research in Washington DC.

So the last thing we want to do as ARPA funders is to try to 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 was say, hey let's not be here for longer than two years. And so every two years, 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. So he was second lieutenant chairing meetings with generals in it. 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 also was 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. He could explain everything that Licklider could do and why it worked.

So here's a couple of things I'm not going to go on about, but basically the idea here is it isn't like let's 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 freaking 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 this unless you have the chops, then you have to make your own hardware and software and operating system and 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 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 Park 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 design a computer that would optimize and make more efficient what you're doing on a super computer. That was what Sketchpad was. Nobody thought that the next graphic systems were gonna be done on 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, had to 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, so it wasn't just the stuff in the past. I'll show you a couple more of those, wow, we're getting close to. But it was creating the next generation. Again, this is baseball.

Baseball, have to develop talent going all the way 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 the 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 like 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 a 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 can go down there and buy almost anything to mess around with. And that group got used to, everybody was broke. So, but you could build your own, like there's 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 and build it.

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

And what happened, the prediction was thirty years and so what happened was very in line with doubling every two years to every eighteen months. And there was physics behind this, this wasn't just an engineering aspiration. And so if you believe this, you had something really worthwhile. I'm gonna skip past angle barking Set it so I see it over 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 would 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 flow charts 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 a hallmark of these people, they generally did it good enough.

Or we may start to edit the flow diagram. First, we erase a flow arrow, then move the connector out of the way so that we may draw a box in its 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 more even about this. This system was 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 when he came back from ARPA was to do this. I worked on this when I was a graduate student. You could grab things that had a thing in your hand. You could grab things and move them around.

It's a little exciting because instead of the thing that you're used to today in VR, it had two CRTs with 15,000 volts right above your ears crackling away. So it's 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 oh 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 the 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, goes down. This is the way people tend to measure things. 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. Reading scores never get above 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 systems 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 gonna work on all of those problems anymore. We're gonna condition the unsophisticated public to do work at the level of a two year old or a 92 year old. And we're just gonna eliminate everything in between.

And the public has bought it because you don't wanna 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 the McCready sweet spot. He's the guy who did man powered flight. And once you have achieved that, it opens up a whole region that you can explore in.

That's what we did at Park. The moon shot was set space travel back fifty years. Everybody uses this 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 Bezos and. Yeah, Elon. They don't get it.

MV equals 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. But the thing that was a tragedy was that there 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 moonshot was not about space travel.

Okay, so I'll skip past this Because I wanna end with, 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 head mounted 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. Greatest hockey player whoever works. And he was just a little guy, he tried to avoid fights. They asked him why he took so many shots on goal. 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 1,000. 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, 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 gonna be and went to that place. So you can make a game to invent the future out of this. So you start off with a cosmic goodness intuition, like for me the tablet one was good.

You identify a favorable exponential, like Moore's Law. You take the cosmic intuition out thirty years and you ask, can we say, wouldn't it be ridiculous if we didn't have this? And see, years out, thirty years away, well of course we'll have one. That's what that exponential means. And bring it back to the ten, fifteen year point.

At 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 ten, fifteen years in the future. That's what the Alto 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 with, so it'll 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 now 5,000,000,000 people. And deal with millions of people who are 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 PARC in 1974.

If you optimize the code, you can get what the applications are gonna be ten years out. So those are the two things you can do by doing this super computer thing. And it costs money. In today's dollars, those Altos cost about 125 ks a piece and we made 2,000 of them. Think about that. Gotta be a funder who's serious, Xerox went batch it when we did it.

They really went batch it when we wanted to cash them in. But I'll just leave you this, since I'm overtime 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 invent the future from the future. You go out and live in the future and bring the future back. Thank you.