[Computer-go] 7.0 Komi and weird deep search result

"Ingo Althöfer" 3-Hirn-Verlag at gmx.de
Thu Apr 7 09:24:55 PDT 2011

Hello Aja,

> ... 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).

Remi was a strong computer chess programmer ("The Crazy Bishop")
before he went to computer go. There is for instance a photo of
him at the WCCC 2004, in the middle of the report


> Aja
>   ----- Original Message ----- 
>   From: Don Dailey 
>   To: Aja 
>   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. 
>   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 ...
>   Don
>     Aja

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