The biggest lesson that can be read from 70 years of AI research is that general methods that leverage computation are ultimately the most effective, and by a large margin.
从 70 年人工智能研究中能读出的最大教训是:利用算力的通用方法终究是最有效的,而且优势巨大。
The ultimate reason for this is Moore's law, or rather its generalization of continued exponentially falling cost per unit of computation.
根本原因是摩尔定律——或者说它的推广形式:单位算力的成本持续呈指数下降。
Most AI research has been conducted as if the computation available to the agent were constant (in which case leveraging human knowledge would be one of the only ways to improve performance) but, over a slightly longer time than a typical research project, massively more computation inevitably becomes available.
大多数 AI 研究做起来,就好像智能体可用的算力是恒定的(果真如此,利用人类知识差不多就是提升性能的唯一途径了)——但只要把时间拉得比一个典型研究项目稍长一点,海量的新增算力就必然到来。
Seeking an improvement that makes a difference in the shorter term, researchers seek to leverage their human knowledge of the domain, but the only thing that matters in the long run is the leveraging of computation.
为了在短期内做出看得见的改进,研究者倾向于利用自己对领域的人类知识;但长期来看,唯一重要的是对算力的利用。
These two need not run counter to each other, but in practice they tend to. Time spent on one is time not spent on the other. There are psychological commitments to investment in one approach or the other.
这两条路本不必相互冲突,但实践中往往冲突:花在一边的时间就不能花在另一边;对某一条路线的投入,会形成心理上的执念。
And the human-knowledge approach tends to complicate methods in ways that make them less suited to taking advantage of general methods leveraging computation.
而且人类知识路线常把方法搞得复杂,反而不利于借助那些利用算力的通用方法。
There were many examples of AI researchers' belated learning of this bitter lesson, and it is instructive to review some of the most prominent.
AI 研究者迟迟才学会这个苦涩教训的例子很多,回顾其中最著名的几个颇有教益。
In computer chess, the methods that defeated the world champion, Kasparov, in 1997, were based on massive, deep search.
在计算机国际象棋领域,1997 年击败世界冠军卡斯帕罗夫的方法,靠的是大规模的深度搜索。
At the time, this was looked upon with dismay by the majority of computer-chess researchers who had pursued methods that leveraged human understanding of the special structure of chess.
当时,大多数研究者一直在钻研如何利用"人类对国际象棋特殊结构的理解",他们对此深感沮丧。
When a simpler, search-based approach with special hardware and software proved vastly more effective, these human-knowledge-based chess researchers were not good losers.
当一个更简单的、基于搜索的方法(配上专用软硬件)被证明远为有效时,这些人类知识派的棋类研究者输得并不体面。
They said that "brute force" search may have won this time, but it was not a general strategy, and anyway it was not how people played chess.
他们说:"暴力"搜索这次也许赢了,但它不是通用策略,况且人类下棋根本不是这么下的。
These researchers wanted methods based on human input to win and were disappointed when they did not.
这些研究者希望获胜的是基于人类输入的方法,未能如愿,便失望不已。
A similar pattern of research progress was seen in computer Go, only delayed by a further 20 years.
计算机围棋上演了相似的剧情,只是又晚了 20 年。
Enormous initial efforts went into avoiding search by taking advantage of human knowledge, or of the special features of the game, but all those efforts proved irrelevant, or worse, once search was applied effectively at scale.
起初,大量精力花在借助人类知识或围棋的特殊性质来避免搜索上;可一旦搜索被有效地大规模应用,那些努力全都变得无关紧要,甚至成了累赘。
Also important was the use of learning by self play to learn a value function (as it was in many other games and even in chess, although learning did not play a big role in the 1997 program that first beat a world champion).
同样重要的是用自我对弈来学习价值函数(许多其他棋类乃至国际象棋也是如此,尽管在 1997 年那个首次击败世界冠军的程序里,学习的作用并不大)。
Learning by self play, and learning in general, is like search in that it enables massive computation to be brought to bear.
自我对弈学习——以及广义的学习——与搜索一样,都能让海量算力派上用场。
Search and learning are the two most important classes of techniques for utilizing massive amounts of computation in AI research.
搜索与学习,是 AI 研究中利用海量算力的两大类最重要的技术。
In computer Go, as in computer chess, researchers' initial effort was directed towards utilizing human understanding (so that less search was needed) and only much later was much greater success had by embracing search and learning.
在计算机围棋中,一如在国际象棋中,研究者最初的努力都指向利用人类理解(以便少用搜索),直到很久之后,拥抱搜索与学习才带来了大得多的成功。
In speech recognition, there was an early competition, sponsored by DARPA, in the 1970s.
语音识别领域,1970 年代有过一场 DARPA 资助的早期竞赛。
Entrants included a host of special methods that took advantage of human knowledge—knowledge of words, of phonemes, of the human vocal tract, etc.
参赛方法中,一大批是利用人类知识的专门方法——关于词、音素、人类声道等等的知识。
On the other side were newer methods that were more statistical in nature and did much more computation, based on hidden Markov models (HMMs).
另一边是更新的方法,更偏统计性质、计算量大得多,基于隐马尔可夫模型(HMM)。
Again, the statistical methods won out over the human-knowledge-based methods.
统计方法再一次胜过了人类知识方法。
This led to a major change in all of natural language processing, gradually over decades, where statistics and computation came to dominate the field.
这引发了整个自然语言处理领域在数十年间的大转向:统计与计算逐渐统治了这个领域。
The recent rise of deep learning in speech recognition is the most recent step in this consistent direction.
近年深度学习在语音识别中的崛起,是这个一贯方向上最新的一步。
Deep learning methods rely even less on human knowledge, and use even more computation, together with learning on huge training sets, to produce dramatically better speech recognition systems.
深度学习方法更少依赖人类知识、动用更多算力,配合在巨型训练集上的学习,造出了好得多的语音识别系统。
As in the games, researchers always tried to make systems that worked the way the researchers thought their own minds worked—they tried to put that knowledge in their systems—but it proved ultimately counterproductive, and a colossal waste of researcher's time, when, through Moore's law, massive computation became available and a means was found to put it to good use.
和棋类一样,研究者总想让系统按照"他们以为自己头脑运作的方式"来工作——想把那种知识装进系统——但当摩尔定律送来海量算力、且人们找到了善用之道时,这一切最终被证明适得其反,是对研究者时间的巨大浪费。
In computer vision, there has been a similar pattern.
计算机视觉如出一辙。
Early methods conceived of vision as searching for edges, or generalized cylinders, or in terms of SIFT features. But today all this is discarded.
早期方法把视觉设想为寻找边缘、寻找广义圆柱体,或者用 SIFT 特征来描述。今天这些全被抛弃了。
Modern deep-learning neural networks use only the notions of convolution and certain kinds of invariances, and perform much better.
现代深度学习神经网络只用到卷积和某几类不变性的概念,效果好得多。
This is a big lesson. As a field, we still have not thoroughly learned it, as we are continuing to make the same kind of mistakes.
这是一个大教训。作为一个领域,我们仍然没有彻底学会它——我们还在犯同一类错误。
To see this, and to effectively resist it, we have to understand the appeal of these mistakes.
要看清这一点并有效抵抗,就必须先理解这类错误的诱人之处。
We have to learn the bitter lesson that building in how we think we think does not work in the long run.
我们必须学会这个苦涩的教训:把"我们以为自己是怎么思考的"内建进系统,长期是行不通的。
The bitter lesson is based on the historical observations that 1) AI researchers have often tried to build knowledge into their agents, 2) this always helps in the short term, and is personally satisfying to the researcher, but 3) in the long run it plateaus and even inhibits further progress, and 4) breakthrough progress eventually arrives by an opposing approach based on scaling computation by search and learning.
苦涩教训基于这样的历史观察:1)AI 研究者总想把知识内建进他们的智能体;2)短期内这总是有效的,而且让研究者个人很有成就感;3)但长期来看它会进入平台期,甚至阻碍进一步发展;4)突破性进展最终来自相反的路线——用搜索与学习去规模化算力。
The eventual success is tinged with bitterness, and often incompletely digested, because it is success over a favored, human-centric approach.
最终的成功总是带着苦味,而且常常没有被完全消化,因为那是对一条人们偏爱的、以人为中心的路线的胜利。
One thing that should be learned from the bitter lesson is the great power of general purpose methods, of methods that continue to scale with increased computation even as the available computation becomes very great.
从苦涩教训中应当学到的第一点,是通用方法的巨大威力——那些在可用算力已经变得很大时,仍能随算力增长而继续变强的方法。
The two methods that seem to scale arbitrarily in this way are search and learning.
看起来能够这样无限扩展的方法有两个:搜索与学习。
The second general point to be learned from the bitter lesson is that the actual contents of minds are tremendously, irredeemably complex; we should stop trying to find simple ways to think about the contents of minds, such as simple ways to think about space, objects, multiple agents, or symmetries.
第二点是:心智的实际内容是极其复杂、无可救药地复杂的;我们应该停止寻找思考心智内容的简单方式——比如关于空间、物体、多智能体或对称性的简单理论。
All these are part of the arbitrary, intrinsically-complex, outside world. They are not what should be built in, as their complexity is endless; instead we should build in only the meta-methods that can find and capture this arbitrary complexity.
这些都属于那个任意的、本质复杂的外部世界。它们不应该被内建进系统,因为其复杂性无穷无尽;我们应该内建的,只有能够发现并捕捉这种任意复杂性的元方法。
Essential to these methods is that they can find good approximations, but the search for them should be by our methods, not by us.
这些方法的关键在于能找到好的近似——但寻找近似这件事,应该交给我们的方法去做,而不是由我们亲自去做。
We want AI agents that can discover like we can, not which contain what we have discovered.
我们想要的是能像我们一样去发现的 AI 智能体,而不是装着我们已有发现的智能体。
Building in our discoveries only makes it harder to see how the discovering process can be done.
把我们的发现内建进去,只会让"发现的过程究竟如何进行"变得更难看清。