苦涩的教训

2019 年 3 月 13 日 March 13, 2019

从 70 年的人工智能研究中可以得出的最大教训是，利用算力的通用方法最终是最有效的，而且优势巨大。其根本原因是摩尔定律，或者更确切地说，是每单位算力成本持续指数下降的普遍化。大多数人工智能研究都是在假设智能体可用的算力是恒定的情况下进行的（在这种情况下，利用人类知识将是提高性能的唯一途径之一），但在比典型研究项目稍长的时间跨度内，大规模更多的算力不可避免地会变得可用。为了在短期内寻求改进，研究人员试图利用他们对领域的人类知识，但从长远来看，唯一重要的是利用算力。这两者并不一定相互对立，但在实践中往往如此。花在一个方面的时间就是花在另一个方面的时间。对某种方法投入存在心理上的承诺。而且，人类知识方法往往会使方法复杂化，从而使其不太适合利用利用算力的通用方法。人工智能研究人员迟迟才学到这个苦涩教训的例子有很多，回顾一些最突出的例子是有启发性的。

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. The ultimate reason for this is Moore's law, or rather its generalization of continued exponentially falling cost per unit of computation. 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. 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. 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. And the human-knowledge approach tends to complicate methods in ways that make them less suited to taking advantage of general methods leveraging computation. There were many examples of AI researchers' belated learning of this bitter lesson, and it is instructive to review some of the most prominent.

在计算机国际象棋中，1997 年击败世界冠军卡斯帕罗夫的方法是基于大规模、深度的搜索。当时，这令大多数追求利用人类对国际象棋特殊结构理解的方法的计算机国际象棋研究人员感到沮丧。当一种更简单的、基于搜索的方法配合专用硬件和软件被证明更有效时，这些基于人类知识的国际象棋研究人员并不甘心失败。他们说“蛮力”搜索这次可能赢了，但这并不是一种通用策略，而且无论如何这不是人类下棋的方式。这些研究人员希望基于人类输入的方法获胜，当它们没有获胜时，他们感到失望。

In computer chess, the methods that defeated the world champion, Kasparov, in 1997, were based on massive, deep search. 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. 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. 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. These researchers wanted methods based on human input to win and were disappointed when they did not.

在计算机围棋中，也出现了类似的研究进展模式，只是推迟了 20 年。最初，人们投入了巨大的努力来避免搜索，利用人类知识或游戏的特性，但所有这些努力都被证明是无关紧要的，甚至更糟，一旦搜索被有效地大规模应用。同样重要的是，通过自我对弈学习价值函数（这在许多其他游戏中也很重要，甚至在象棋中也是如此，尽管学习在 1997 年首次击败世界冠军的程序中并没有发挥重要作用）。自我对弈学习和一般的学习，就像搜索一样，使得大规模算力得以发挥作用。搜索和学习是利用人工智能研究中大量算力的两类最重要的技术。在计算机围棋中，就像在计算机国际象棋中一样，研究人员最初的努力方向是利用人类理解（以便减少搜索），直到很久以后，通过拥抱搜索和学习才取得了更大的成功。

A similar pattern of research progress was seen in computer Go, only delayed by a further 20 years. 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. 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). Learning by self play, and learning in general, is like search in that it enables massive computation to be brought to bear. Search and learning are the two most important classes of techniques for utilizing massive amounts of computation in AI research. 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.

在语音识别领域，20 世纪 70 年代 DARPA 赞助了一场早期竞赛。参赛者包括许多利用人类知识的方法——关于单词、音素、人类声道等的知识。另一方面是更新的方法，这些方法更具统计性质，并进行了更多的计算，基于隐马尔可夫模型（HMM）。同样，统计方法战胜了基于人类知识的方法。这导致了整个自然语言处理领域的重大变化，在几十年的时间里，统计和计算逐渐主导了该领域。最近深度学习在语音识别中的兴起是这一持续方向的最新一步。深度学习方法更少依赖人类知识，使用更多计算，结合大规模训练集上的学习，产生了显著更好的语音识别系统。就像在游戏中一样，研究人员总是试图让系统按照他们认为自己思维运作的方式工作——他们试图将这些知识放入系统中——但事实证明这最终适得其反，并且浪费了研究人员的巨大时间，当通过摩尔定律，大规模算力变得可用并且找到了有效利用它的方法时。

In speech recognition, there was an early competition, sponsored by DARPA, in the 1970s. Entrants included a host of special methods that took advantage of human knowledge---knowledge of words, of phonemes, of the human vocal tract, etc. On the other side were newer methods that were more statistical in nature and did much more computation, based on hidden Markov models (HMMs). Again, the statistical methods won out over the human-knowledge-based methods. This led to a major change in all of natural language processing, gradually over decades, where statistics and computation came to dominate the field. The recent rise of deep learning in speech recognition is the most recent step in this consistent direction. 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. 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.

在计算机视觉领域，也出现了类似的模式。早期方法将视觉视为寻找边缘、广义圆柱体或 SIFT 特征。但今天所有这些都被抛弃了。现代深度学习神经网络只使用卷积和某些不变性的概念，并且表现好得多。

In computer vision, there has been a similar pattern. Early methods conceived of vision as searching for edges, or generalized cylinders, or in terms of SIFT features. But today all this is discarded. Modern deep-learning neural networks use only the notions of convolution and certain kinds of invariances, and perform much better.

这是一个重要的教训。作为一个领域，我们还没有完全吸取这个教训，因为我们仍在犯同样的错误。要看到这一点，并有效地抵制它，我们必须理解这些错误的吸引力。我们必须学会这个苦涩的教训：将我们认为的思维方式内置到系统中，从长远来看是行不通的。这个苦涩的教训基于历史观察：1）人工智能研究人员经常试图将知识构建到他们的智能体中；2）这在短期内总是有帮助的，并且对研究人员个人来说令人满意；3）但从长远来看，它会达到平台期，甚至阻碍进一步进展；4）突破性进展最终通过基于搜索和学习的算力扩展的相反方法实现。最终的成功带有苦涩，并且常常没有被完全消化，因为这是对一种以人为中心的方法的成功。

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. To see this, and to effectively resist it, we have to understand the appeal of these mistakes. We have to learn the bitter lesson that building in how we think we think does not work in the long run. 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. The eventual success is tinged with bitterness, and often incompletely digested, because it is success over a favored, human-centric approach.

从苦涩的教训中应该学到的一点是通用方法的巨大力量，这些方法随着可用算力的增加而持续扩展，即使可用算力变得非常大。似乎能够以这种方式任意扩展的两种方法是搜索和学习。

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. The two methods that seem to scale arbitrarily in this way are search and learning.

从苦涩的教训中学到的第二个普遍观点是，思维的实际内容极其复杂，无法简化；我们应该停止试图找到思考思维内容的简单方法，例如思考空间、物体、多个智能体或对称性的简单方法。所有这些都是任意的、内在复杂的外部世界的一部分。它们不应该被内置，因为它们的复杂性是无穷无尽的；相反，我们应该只内置能够发现并捕捉这种任意复杂性的元方法。这些方法的关键在于它们能够找到良好的近似，但寻找这些近似应该由我们的方法来完成，而不是由我们直接完成。我们希望人工智能智能体能够像我们一样发现，而不是包含我们已经发现的东西。将我们的发现内置进去只会让我们更难看到发现过程是如何完成的。

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. 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. Essential to these methods is that they can find good approximations, but the search for them should be by our methods, not by us. We want AI agents that can discover like we can, not which contain what we have discovered. Building in our discoveries only makes it harder to see how the discovering process can be done.