Artificial Intelligence—The revolution hasn’t happened yet
Michael I. Jordan, Amazon scholar and professor at the University of California, Berkeley, writes about the classical goals in human-imitative AI, and reflects on how in the current hubbub over the AI revolution it is easy to forget that these goals haven’t yet been achieved. This article is reprinted with permission from the Harvard Data Science Review, where it first appeared.
Artificial Intelligence (AI) is the mantra of the current era. The phrase is intoned by technologists, academicians, journalists, and venture capitalists alike. As with many phrases that cross over from technical academic fields into general circulation, there is significant misunderstanding accompanying use of the phrase. However, this is not the classical case of the public not understanding the scientists—here the scientists are often as befuddled as the public. The idea that our era is somehow seeing the emergence of an intelligence in silicon that rivals our own entertains all of us, enthralling us and frightening us in equal measure. And, unfortunately, it distracts us.
There is a different narrative that one can tell about the current era. Consider the following story, which involves humans, computers, data, and life-or-death decisions, but where the focus is something other than intelligence-in-silicon fantasies. When my spouse was pregnant 14 years ago, we had an ultrasound. There was a geneticist in the room, and she pointed out some white spots around the heart of the fetus. “Those are markers for Down syndrome,” she noted, “and your risk has now gone up to one in 20.” She let us know that we could learn whether the fetus in fact had the genetic modification underlying Down syndrome via an amniocentesis, but amniocentesis was risky—the chance of killing the fetus during the procedure was roughly one in 300. Being a statistician, I was determined to find out where these numbers were coming from. In my research, I discovered that a statistical analysis had been done a decade previously in the UK in which these white spots, which reflect calcium buildup, were indeed established as a predictor of Down syndrome. I also noticed that the imaging machine used in our test had a few hundred more pixels per square inch than the machine used in the UK study. I returned to tell the geneticist that I believed that the white spots were likely false positives, literal white noise.
She said, “Ah, that explains why we started seeing an uptick in Down syndrome diagnoses a few years ago. That’s when the new machine arrived.”
We didn’t do the amniocentesis, and my wife delivered a healthy girl a few months later, but the episode troubled me, particularly after a back-of-the-envelope calculation convinced me that many thousands of people had gotten that diagnosis that same day worldwide, that many of them had opted for amniocentesis, and that a number of babies had died needlessly. The problem that this episode revealed wasn’t about my individual medical care; it was about a medical system that measured variables and outcomes in various places and times, conducted statistical analyses, and made use of the results in other situations. The problem had to do not just with data analysis per se, but with what database researchers call provenance—broadly, where did data arise, what inferences were drawn from the data, and how relevant are those inferences to the present situation? While a trained human might be able to work all of this out on a case-by-case basis, the issue was that of designing a planetary-scale medical system that could do this without the need for such detailed human oversight.
I’m also a computer scientist, and it occurred to me that the principles needed to build planetary-scale inference-and-decision-making systems of this kind, blending computer science with statistics, and considering human utilities, were nowhere to be found in my education. It occurred to me that the development of such principles—which will be needed not only in the medical domain but also in domains such as commerce, transportation, and education—were at least as important as those of building AI systems that can dazzle us with their game-playing or sensorimotor skills.
Whether or not we come to understand ‘intelligence’ any time soon, we do have a major challenge on our hands in bringing together computers and humans in ways that enhance human life. While some view this challenge as subservient to the creation of artificial intelligence, another more prosaic, but no less reverent, viewpoint is that it is the creation of a new branch of engineering. Much like civil engineering and chemical engineering in decades past, this new discipline aims to corral the power of a few key ideas, bringing new resources and capabilities to people, and to do so safely. Whereas civil engineering and chemical engineering built upon physics and chemistry, this new engineering discipline will build on ideas that the preceding century gave substance to, such as information, algorithm, data, uncertainty, computing, inference, and optimization. Moreover, since much of the focus of the new discipline will be on data from and about humans, its development will require perspectives from the social sciences and humanities.
While the building blocks are in place, the principles for putting these blocks together are not, and so the blocks are currently being put together in ad-hoc ways. Thus, just as humans built buildings and bridges before there was civil engineering, humans are proceeding with the building of societal-scale, inference-and-decision-making systems that involve machines, humans, and the environment. Just as early buildings and bridges sometimes fell to the ground—in unforeseen ways and with tragic consequences—many of our early societal-scale inference-and-decision-making systems are already exposing serious conceptual flaws.
Unfortunately, we are not very good at anticipating what the next emerging serious flaw will be. What we’re missing is an engineering discipline with principles of analysis and design.
The current public dialog about these issues too often uses the term AI as an intellectual wildcard, one that makes it difficult to reason about the scope and consequences of emerging technology. Let us consider more carefully what AI has been used to refer to, both recently and historically.
Most of what is labeled AI today, particularly in the public sphere, is actually machine learning (ML), a term in use for the past several decades. ML is an algorithmic field that blends ideas from statistics, computer science and many other disciplines (see below) to design algorithms that process data, make predictions, and help make decisions. In terms of impact on the real world, ML is the real thing, and not just recently. Indeed, that ML would grow into massive industrial relevance was already clear in the early 1990s, and by the turn of the century forward-looking companies such as Amazon were already using ML throughout their business, solving mission-critical, back-end problems in fraud detection and supply-chain prediction, and building innovative consumer-facing services such as recommendation systems. As datasets and computing resources grew rapidly over the ensuing two decades, it became clear that ML would soon power not only Amazon but essentially any company in which decisions could be tied to large-scale data. New business models would emerge. The phrase ‘data science’ emerged to refer to this phenomenon, reflecting both the need of ML algorithms experts to partner with database and distributed-systems experts to build scalable, robust ML systems, as well as reflecting the larger social and environmental scope of the resulting systems.This confluence of ideas and technology trends has been rebranded as ‘AI’ over the past few years. This rebranding deserves some scrutiny.
Historically, the phrase “artificial intelligence” was coined in the late 1950s to refer to the heady aspiration of realizing in software and hardware an entity possessing human-level intelligence. I will use the phrase “human-imitative AI” to refer to this aspiration, emphasizing the notion that the artificially intelligent entity should seem to be one of us, if not physically then at least mentally (whatever that might mean). This was largely an academic enterprise. While related academic fields such as operations research, statistics, pattern recognition, information theory, and control theory already existed, and often took inspiration from human or animal behavior, these fields were arguably focused on low-level signals and decisions. The ability of, say, a squirrel to perceive the three-dimensional structure of the forest it lives in, and to leap among its branches, was inspirational to these fields. AI was meant to focus on something different: the high-level or cognitive capability of humans to reason and to think. Sixty years later, however, high-level reasoning and thought remain elusive. The developments now being called AI arose mostly in the engineering fields associated with low-level pattern recognition and movement control, as well as in the field of statistics, the discipline focused on finding patterns in data and on making well-founded predictions, tests of hypotheses, and decisions.
Indeed, the famous backpropagation algorithm that David Rumelhart rediscovered in the early 1980s, and which is now considered at the core of the so-called “AI revolution,” first arose in the field of control theory in the 1950s and 1960s. One of its early applications was to optimize the thrusts of the Apollo spaceships as they headed towards the moon.
Since the 1960s, much progress has been made, but it has arguably not come about from the pursuit of human-imitative AI. Rather, as in the case of the Apollo spaceships, these ideas have often hidden behind the scenes, the handiwork of researchers focused on specific engineering challenges. Although not visible to the general public, research and systems-building in areas such as document retrieval, text classification, fraud detection, recommendation systems, personalized search, social network analysis, planning, diagnostics, and A/B testing have been a major success—these advances have powered companies such as Google, Netflix, Facebook, and Amazon.
One could simply refer to all of this as AI, and indeed that is what appears to have happened. Such labeling may come as a surprise to optimization or statistics researchers, who find themselves suddenly called AI researchers, but labels aside, the bigger problem is that the use of this single, ill-defined acronym prevents a clear understanding of the range of intellectual and commercial issues at play.
The past two decades have seen major progress—in industry and academia—in a complementary aspiration to human-imitative AI that is often referred to as “Intelligence Augmentation” (IA). Here computation and data are used to create services that augment human intelligence and creativity. A search engine can be viewed as an example of IA, as it augments human memory and factual knowledge, as can natural language translation, which augments the ability of a human to communicate. Computer-based generation of sounds and images serves as a palette and creativity enhancer for artists. While services of this kind could conceivably involve high-level reasoning and thought, currently they don’t; they mostly perform various kinds of string-matching and numerical operations that capture patterns that humans can make use of.
Hoping that the reader will tolerate one last acronym, let us conceive broadly of a discipline of “Intelligent Infrastructure” (II), whereby a web of computation, data, and physical entities exists that makes human environments more supportive, interesting, and safe. Such infrastructure is beginning to make its appearance in domains such as transportation, medicine, commerce, and finance, with implications for individual humans and societies. This emergence sometimes arises in conversations about an Internet of Things, but that effort generally refers to the mere problem of getting ‘things’ onto the Internet, not to the far grander set of challenges associated with building systems that analyze those data streams to discover facts about the world and permit ‘things’ to interact with humans at a far higher level of abstraction than mere bits.
For example, returning to my personal anecdote, we might imagine living our lives in a societal-scale medical system that sets up data flows and data-analysis flows between doctors and devices positioned in and around human bodies, thereby able to aid human intelligence in making diagnoses and providing care. The system would incorporate information from cells in the body, DNA, blood tests, environment, population genetics, and the vast scientific literature on drugs and treatments. It would not just focus on a single patient and a doctor, but on relationships among all humans, just as current medical testing allows experiments done on one set of humans (or animals) to be brought to bear in the care of other humans. It would help maintain notions of relevance, provenance, and reliability, in the way that the current banking system focuses on such challenges in the domain of finance and payment. While one can foresee many problems arising in such a system—privacy issues, liability issues, security issues, etc.—these concerns should be viewed as challenges, not show-stoppers.
We now come to a critical issue: is working on classical human-imitative AI the best or only way to focus on these larger challenges? Some of the most heralded recent success stories of ML have in fact been in areas associated with human-imitative AI—areas such as computer vision, speech recognition, game-playing, and robotics. Perhaps we should simply await further progress in domains such as these. There are two points to make here. First, although one would not know it from reading the newspapers, success in human-imitative AI has in fact been limited; we are very far from realizing human-imitative AI aspirations. The thrill (and fear) of making even limited progress on human-imitative AI gives rise to levels of over-exuberance and media attention that is not present in other areas of engineering.
Second, and more importantly, success in these domains is neither sufficient nor necessary to solve important IA and II problems. On the sufficiency side, consider self-driving cars. For such technology to be realized, a range of engineering problems will need to be solved that may have little relationship to human competencies (or human lack-of-competencies). The overall transportation system (an II system) will likely more closely resemble the current air-traffic control system than the current collection of loosely coupled, forward-facing, inattentive human drivers. It will be vastly more complex than the current air-traffic control system, specifically in its use of massive amounts of data and adaptive statistical modeling to inform fine-grained decisions. Those challenges need to be in the forefront versus a potentially distracting focus on human-imitative AI.
As for the necessity argument, some say that the human-imitative AI aspiration subsumes IA and II aspirations, because a human-imitative AI system would not only be able to solve the classical problems of AI (e.g., as embodied in the Turing test), but it would also be our best bet for solving IA and II problems. Such an argument has little historical precedent. Did civil engineering develop by envisaging the creation of an artificial carpenter or bricklayer? Should chemical engineering have been framed in terms of creating an artificial chemist? Even more polemically: if our goal was to build chemical factories, should we have first created an artificial chemist who would have then worked out how to build a chemical factory?
A related argument is that human intelligence is the only kind of intelligence we know, thus we should aim to mimic it as a first step. However, humans are in fact not very good at some kinds of reasoning—we have our lapses, biases, and limitations. Moreover, critically, we did not evolve to perform the kinds of large-scale decision-making that modern II systems must face, nor to cope with the kinds of uncertainty that arise in II contexts. One could argue that an AI system would not only imitate human intelligence, but also correct it, and would also scale to arbitrarily large problems. Of course, we are now in the realm of science fiction—such speculative arguments, while entertaining in the setting of fiction, should not be our principal strategy going forward in the face of the critical IA and II problems that are beginning to emerge. We need to solve IA and II problems on their own merits, not as a mere corollary to a human-imitative AI agenda.
It is not hard to pinpoint algorithmic and infrastructure challenges in II systems that are not central themes in human-imitative AI research. II systems require the ability to manage distributed repositories of knowledge that are rapidly changing and are likely to be globally incoherent. Such systems must cope with cloud-edge interactions in making timely, distributed decisions, and they must deal with long-tail phenomena where there is lots of data on some individuals and little data on most individuals. They must address the difficulties of sharing data across administrative and competitive boundaries. Finally, and of particular importance, II systems must bring economic ideas such as incentives and pricing into the realm of the statistical and computational infrastructures that link humans to each other and to valued goods. Such II systems can be viewed as not merely providing a service, but as creating markets. There are domains such as music, literature, and journalism that are crying out for the emergence of such markets, where data analysis links producers and consumers. And this must all be done within the context of evolving societal, ethical, and legal norms.
Of course, classical human-imitative AI problems remain of great interest as well. However, the current focus on doing AI research via the gathering of data, the deployment of deep learning infrastructure, and the demonstration of systems that mimic certain narrowly defined human skills—with little in the way of emerging explanatory principles—tends to deflect attention from major open problems in classical AI. These problems include the need to bring meaning and reasoning into systems that perform natural language processing, the need to infer and represent causality, the need to develop computationally tractable representations of uncertainty and the need to develop systems that formulate and pursue long-term goals. These are classical goals in human-imitative AI, but in the current hubbub over the AI revolution it is easy to forget that they are not yet solved.
IA will also remain quite essential, because for the foreseeable future, computers will not be able to match humans in their ability to reason abstractly about real-world situations. We will need well-thought-out interactions of humans and computers to solve our most pressing problems. And we will want computers to trigger new levels of human creativity, not replace human creativity (whatever that might mean).
It was John McCarthy (while a professor at Dartmouth, and soon to take a position at MIT) who coined the term AI, apparently to distinguish his budding research agenda from that of Norbert Wiener (then an older professor at MIT). Wiener had coined “cybernetics” to refer to his own vision of intelligent systems—a vision that was closely tied to operations research, statistics, pattern recognition, information theory, and control theory. McCarthy, on the other hand, emphasized the ties to logic. In an interesting reversal, it is Wiener’s intellectual agenda that has come to dominate in the current era, under the banner of McCarthy’s terminology. (This state of affairs is surely, however, only temporary; the pendulum swings more in AI than in most fields.)
Beyond the historical perspectives of McCarthy and Wiener, we need to realize that the current public dialog on AI—which focuses on narrow subsets of both industry and of academia—risks blinding us to the challenges and opportunities that are presented by the full scope of AI, IA, and II.
This scope is less about the realization of science-fiction dreams or superhuman nightmares, and more about the need for humans to understand and shape technology as it becomes ever more present and influential in their daily lives. Moreover, in this understanding and shaping, there is a need for a diverse set of voices from all walks of life, not merely a dialog among the technologically attuned. Focusing narrowly on human-imitative AI prevents an appropriately wide range of voices from being heard.
While industry will drive many developments, academia will also play an essential role, not only in providing some of the most innovative technical ideas, but also in bringing researchers from the computational and statistical disciplines together with researchers from other disciplines whose contributions and perspectives are sorely needed—notably the social sciences, the cognitive sciences, and the humanities.
On the other hand, while the humanities and the sciences are essential as we go forward, we should also not pretend that we are talking about something other than an engineering effort of unprecedented scale and scope; society is aiming to build new kinds of artifacts. These artifacts should be built to work as claimed. We do not want to build systems that help us with medical treatments, transportation options, and commercial opportunities only to find out after the fact that these systems don’t really work, that they make errors that take their toll in terms of human lives and happiness. In this regard, as I have emphasized, there is an engineering discipline yet to emerge for the data- and learning-focused fields. As exciting as these latter fields appear to be, they cannot yet be viewed as constituting an engineering discipline.
We should embrace the fact that we are witnessing the creation of a new branch of engineering. The term engineering has connotations—in academia and beyond—of cold, affectless machinery, and of loss of control for humans, but an engineering discipline can be what we want it to be. In the current era, we have a real opportunity to conceive of something historically new: a human-centric engineering discipline. I will resist giving this emerging discipline a name, but if the acronym AI continues to serve as placeholder nomenclature going forward, let’s be aware of the very real limitations of this placeholder. Let’s broaden our scope, tone down the hype, and recognize the serious challenges ahead.