[Computer-go] 7.0 Komi and weird deep search result
michaelwilliams75 at gmail.com
Wed Apr 6 17:23:29 PDT 2011
Personally, I think the whole MCTS strategy is still in it's infancy.
Surely there is still lots of room for improvement in playouts and to a
lesser degree, in-tree move selection.
On Wed, Apr 6, 2011 at 8:08 PM, Aja <ajahuang at gmail.com> wrote:
> Hi Don,
> I don't think you were "rambling on". Your words are informative and
> constructive to me (especially you have very strong background and
> experience from computer chess). Specifically, I am reminded that "computer
> go is still in it's infancy and we are still looking for the big fixes and
> have not yet come to fully appreciate the immense practical power of
> incremental improvements over time." Also, I will be more careful in
> measuring the improvement, as exampled a lot in your description (my
> supervisor Remi Coulom also repeatedly corrects me at this point).
> ----- Original Message -----
> *From:* Don Dailey <dailey.don at gmail.com>
> *To:* Aja <ajahuang at gmail.com>
> *Cc:* computer-go at dvandva.org
> *Sent:* Wednesday, April 06, 2011 9:51 PM
> *Subject:* Re: [Computer-go] 7.0 Komi and weird deep search result
> On Wed, Apr 6, 2011 at 3:32 AM, Aja <ajahuang at gmail.com> wrote:
>> Hi Don,
>> Thanks for your
>> penetrating ideas. Yes, I would like to reconsider my feeling and hope
>> that it doesn’t misguide anyone.
>> We both know the recent controversy between Fruit and Rybka (or Fabien and
>> Vasik), but of course it’s not the issue here right now. Just want to
>> mention in passing that Fabien said he might develop a Go program in the
>> next few years, so we can expect for another open-source strong program.
> I hope he does, but of course I did not bring this up to talk about the
> controversy, just the reality that computer chess software is marching on
> at a remarkable pace and this was an excellent example to illustrate that.
>> It’s just my guess that it’s very hard for current MCTS to surpass amateur
>> 5d or 6d. One main reason is it’s difficult to solve a lot of different
>> semeai and life-and-death instances in pro level, even if the program is
>> running on a super big hardware (by this point I was impressed by Olivier’s
>> talk in a conference of Taiwan, in which he gave an “easy” semeai example
>> that Mogo cannot solve with very larger number of simulations).
> I want to point out that in computer chess that this same exact thing was
> often done not so many years ago. A relatively simple position would be
> presented that humans easily understood, but seemed completely out of reach
> for computer chess programs to understand. It was easy to see that
> computers would need some ridiculous breakthroughs to be able to understand
> such positions and the conclusion was that computers probably would never be
> close to the top humans in chess.
> It's my view that such illustrations tended to cause people to draw the
> wrong conclusions and sent people off in the wrong direction, looking for
> non-existent breakthroughs and concluding that incremental progress was a
> completely foolish way to proceed.
> I believe we (as humans) lack a bit of imagination when it comes to these
> sort of things. For example the 4 minute mile was consider
> physiologically unattainable a few years before the first one was run - in
> other words it was hard to imagine it ever happening. It's often
> difficult for us to imagine things that are too different from what we are
> currently experiencing (especially once we decide it is "hard.") Maybe
> part of the problem is that we live in an instant gratification society and
> no longer think in terms of hard work and gradual progress, we want an
> instant "breakthrough."
> Progress is a funny thing if you put numbers on it. If you get 1%, it
> doesn't seem like hardly anything. But if you add 1% to that, then 1% again,
> it's like compound interest in a bank and you look back over just a few of
> these and are surprised by how much progress you make.
> I have been surprised that in chess the point of diminishing returns is
> farther away that it seems and I'm sure in GO it is even more so by a large
> degree. In other words ELO progress in software has been more or less
> steady, not slowing to a crawl. Yes, it is punctuated with small spikes
> but seen over anything more than a couple of years it's remarkably smooth.
> As evidence of that, the program Houdini recently was released that is at
> least 50 ELO over it's nearest competitor, but you can be sure that is only
> a temporary situation - it will look like a weak program in 2 or 3 years.
>> Another aspect is that it’s extremely hard for MCTS to consider/argue
>> for few points in early stages on 19x19 (because it only sees winning rate
>> and dynamic komi is far from enough to fix it) and that is exactly what pros
>> are very able to.
> The only thing you are telling me is that we picked a hard problem. There
> is nothing here inherently unsolvable, we are just impatient and cannot
> imagine (yet) how we are going to solve this.
> I have discovered that in computer chess (which I have been into for
> decades) the "unsolvable" problems didn't really make that much difference
> in the short term. The solutions come at a natural rate and until
> programs get a lot better in other areas you will find that some of these
> "glaring" weaknesses do not make much different in terms of how strong the
> program is at the moment even when it seems like its a huge deal. These
> weaknesses gradually start making a huge difference when the program is
> really good and we tend to judge programs more by their weaknesses than
> their strengths. So when we see something "ugly" it makes us think the
> program cannot be as strong as it actually has proved to be. And computer
> program have strengths and weakness in different proportions than we do so
> this tends to distort our own views of how good or bad they play.
> An example in computer chess is basic endgame knowledge. It's really ugly
> to see a chess program trade down from a won ending to a draw because it
> doesn't understand that certain simple endings cannot be won despite being a
> piece up. Years ago, after seeing glaring example of this horrible weakness,
> I took some time and implemented a large number of scoring corrections to
> deal with this as well as putting in king and pawn versus king perfect play
> database. I patted myself on the back and expect to see a decent ELO gain.
> However even on modern programs this probably does not add more than 2 or
> 3 ELO and I'm being generous. If you show a grandmaster some of these
> glitches he might conclude that your program plays like an amateur (in fact
> when programs first became master strength many strong human players would
> see one of the "ugly" moves and conclude that the program could not play a
> move like that and even be "expert" strength, let alone master strength.)
> I'm not saying these are not real problem in computer go, but the point is
> that there a large number of problems that altogether define exactly where
> we stand right now and we just have to start making dents (which we actually
> have been doing to a remarkable degree if you would only look more
> carefully.) The bigger problems are just going to take longer to fix than
> the lesser problems. Also, I believe we have to get over this notion
> that we have to "fix it" completely. We probably will not fix it suddenly
> with a one line program change, but we can and will find ways to minimize
> the problems, and it may be gradual and incremental.
> In your example you rightly note that program do very well when in their
> "sweet spot", when there are clearly defined goals that affect winning
> percentages. In computer chess it used to be believed that no amount of
> searching could improve the programs "horrible" positional play and that
> computers only played well if there were immediate tactical considerations,
> otherwise they quickly went wrong. That turned out not to be true, it
> was just not clearly understood at the time because we were looking at the
> problem through our own biased eyes and seeing the ugly things. The
> truth of the matter is that the tree search and playouts works well in all
> positions but some more than others and we will find ways to clearly improve
> the situation in the future with incremental progress (not major
> breakthroughs.) Also, we have some clearly wrong things that we will fix
> (like eye definitions we have are approximations and are sometimes broken.)
> I'll say it again, I think computer go is still in it's infancy and we are
> still looking for the big fixes and have not yet come to fully appreciate
> the immense practical power of incremental improvements over time. When
> the problem looks big we feel like small improvements are a waste of time
> but nothing is farther from the truth.
>> The progress in hardware by Mogo, Fuego and pachi is well-known and
>> impressive, so that I don’t think the amazing progress in computer Go is
>> mainly due to software. Both hardware and software are important in making a
>> strong Go program for now, as far as I can see.
> I think the pattern is the same as it happened in computer chess. But I
> personally believe that software will be a much bigger contributor to
> progress in the future (even if you ignore the "slowdown" of Moores law.)
>> I hope your prediction is right: “without anything really major (but no
>> doubt some new small ideas) we are going to see your KGS 5 and 6 dan and
>> much higher in 5 to 10 years.” If not, then we will have a lot of
>> “interesting” work to do, no matter testing methodology, engineering or
>> academic etc. [image: 微笑]
> I am convinced I am right on this one. I have absolutely nothing against
> finding major breakthroughs of course but I think what we will call
> "breakthroughs" will be things that add up to 50 ELO or less. In chess it
> was things like check extensions, null move pruning, futility pruning, LMR
> etc. We called null move pruning a "major breakthrough" but when it was
> first used it added something like 40 or 50 ELO to the strength of a chess
> program. Is that a major breakthrough? You don't notice 50 ELO right
> away by watching it play because it still will lose 43 percent of the games
> and thus still get outplayed in many games, but It depends on your
> definition of "major" I guess. In go that would be something like 1/2
> dan. I do think there will be a few of these kinds of breakthroughs.
> What happens is that these good ideas need to get refined and improved too.
> I think we get much more out of null move pruning than we used to. LMR
> when first implemented does not give chess program hardly any gain until
> it's done just right. But when refined it's pretty huge. My first LMR
> implementation was only about 20, now it's like 100 ELO or more.
> Thanks for listening to me ramble on about this ...
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