Comment by alankay1 | Hacker News Reader

Comment by alankay1 | Hacker News Reader

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"Cops need criminals"

"Doctors need disease"

Things have happened in the past when passionate and confident people with chops have decided to do something. These have not always correlated with "What is actually needed" (often not) but they usually get things into a state where people who are mainly trying to advance their own goals see some advantage (including "tech chic").

We are certainly not in a position where this can't happen a few more times.

Looking back, I've been struck not by how few really good researchers there are, but more so by how few really good managers of researchers there have been, and even more so by how really really few good funders there have been.

Maybe too simplistic, but in my view great funding has caused great stuff. So the funders should get the gold medals rather than the researchers! (Think about it: the good funders give out the gold in advance knowing full well that if even if they are very luckly 70% of the gold will turn to lead in just a few years!)

few really good managers of researchers

Bob Taylor has been generally praised as a great manager, and I believe them of course. But when I heard stories of his management style, it seemed to go against every instinct we have on how to foster creativity. Could you comment on that?

Also, in terms of funding, I wonder -- haven't things changed? Wasn't funding more important in, say, the 1960's and 70's due to the cost of computer time, especially at the processing level that would let you "see the future." A $1000 computer today is not so different, in terms of power, from a similar machine 5 years ago, right?

Things have happened in the past when passionate and confident people with chops have decided to do something.

But wasn't the past more open? When a field is just forming, everything is crazy, so nothing is. It's only when it has solidified (and in exactly the wrong direction) that you would more expect to find a "crazy professor" having more of an impact, right?

As Alan has said, the importance of funding is more about finding the problem. There's a lot of wandering and false leads involved (though, finding out the false leads is nevertheless valuable. It's still new knowledge). In terms of hardware, the thing to anticipate is what computing power will be necessary for accomplishing things decades from now, and paying the bill for that, not considering what one can buy from a computer retailer today, because that doesn't create the excuse to think of what computers will be able to do.

Using funding to find the problem is inefficient; side projects are a much more distributed and efficient method and they don't need funding.

As for hardware, you're repeating what's clear. What I'm saying is that you used to have to purchase the future but now you can mimic those coming changes and, while slower, offer perfectly acceptable performance.

I guess I'm trying to lead Alan to say something to the effect that the next PARC can be groups, working together, on their own time, over Skype. I'm not sure he believes that but I do.

Tell me the stories, and I'll comment on them.

If you are computing on a $1000 computer, you are computing in the past. Part of the idea here is that you want to do research and development on supercomputers of the present that will give you the resources that will be available at lower prices in the future.

With salaries as they are today -- and real estate much worse -- it is actually more expensive to fund the same kinds of research today.

The past was similar to today in that most people in computing back then were orbiting around some local vendor's and local fads notions of computing. And it was a lot harder to make computers and other tools back then. It wasn't a crazy professor having an impact back then, but a whole research community that was required to make an impact.

The stories I know came from Dealers of Lightning and what I remember (correctly I hope) is that the weekly meetings were quite contentious and that he would even encourage haranguing the presenter. Is that true? Did the people there feel it as healthy constructive criticism? I would worry that this would more likely stifle creative thought than encourage it.

If you are computing on a $1000 computer, you are computing in the past.

I know that this was true in the past but it's my contention that hardware has had Moore's Law where software has stagnated, and that the passing of time has meant that now current software doesn't often take full advantage of the hardware available. If you did architect based on where the puck is going (optimized for multi-core, no main memory) current hardware wouldn't slow you down the same way as it did before and sometimes you would even see a performance gain.

By the way, thanks for doing this.

The research community was "an arguing community", and knew how to argue "in good ways" (i.e. no personal attacks, only trying to illuminate the issues, etc.) This worked pretty well almost always ... (The weekly meetings were not for being creative, but for discussion ...)

Let me respectfully disagree with your contention. The point that is missed is not what the hardware could do, but what can you do without optimizing. It is very very hard to put on the optimization hat without removing the design hat, and once you've removed the latter you are lost.

The key to the Parc approach was to be able to do many experiments in the future without having to optimize. (There was a second part to this "key" but I'll omit it here)

I should have assumed, given the results that PARC had, that it must have been that way. It's fantastic that I just got the answer to that question from... you.

For my second point -- I definitely didn't mean optimization that way. I guess the word I meant to use was "targeted", as in "targeted for multi-core" but I see your point and respect it fully.

I'm thrilled and deeply, deeply honored to have had this time with you, Dr. Kay. Thank you so much again. If you're ever in the Bay Area on the first Saturday of the month and feel inclined to stop briefly by the 2020 group meeting (which is an attempt at a replacement for the Future of Programming Workshops that used to take place at Strange Loop), we would be over the moon. You can reach out to Jonathan Edwards if you need the details.

The basic principle of both points above is that "problem finding" is the hardest thing in "real research", so a lot of things need to be done to help this ... (this is a very tough sell and even "explain" today -- almost everyone is brought up -- especially in schools -- to solve problems, rather than to actually find good ones) -- and virtually all funders today want to know what problems their fundees are going to solve - so they underfund (to the point of 0!) the finding processes ...

The ARPA/Parc process "funded people, not projects" -- and today this seems quite outre to most.

As you probably know, Jonathan is doing some work with us ...

Yes I know about Jonathan, which is why I mentioned him because I didn't want to publish the details of the group here and he's been something like an adviser to the group.

And that group is probably also the reasons for my views. I would never qualify to be in HARC and yet I don't just want to be content to scorn the state of the industry and state of the art. I see that there's additionally interesting research coming from garages and weekend projects. I feel that "problem finding" is somewhat interchangeable with "point of view" and that can come from surprising sources. Funding might be needed for the hardware but my own experience, for what it's worth, hasn't borne that out. The main component then is time, and while weekends aren't much, they'll have to suffice. The last step is to see if we can't get further as a community, giving that feedback so critical at PARC, and so that is why the group was created.

Better to invent the electric light bulb than to cope with candles ... ?

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