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Headroom for AI development

(Dylan Foster and Alex Lamb both helped in creating this.)

In thinking about what are good research problems, it’s sometimes helpful to switch from what is understood to what is clearly possible. This encourages us to think beyond simply improving the existing system. For example, we have seen instances throughout the history of machine learning where researchers have argued for fixing an architecture and using it for short-term success, ignoring potential for long-term disruption. As an example, the speech recognition community spent decades focusing on Hidden Markov Models at the expense of other architectures, before eventually being disrupted by advancements in deep learning. Support Vector Machines were disrupted by deep learning, and convolutional neural networks were displaced by transformers. This pattern may repeat for the current transformer/large language model (LLM) paradigm. Here are some quick calculations suggesting it may be possible to do significantly better along multiple axes. Examples include the following:

  • Language learning efficiency: A human baby can learn a good model for human language after observing 0.01% of the language tokens typically used to train a large language model.
  • Representational efficiency: A tiny Portia spider with a brain a million times smaller than a human can plan a course of action and execute it over the course of an hour to catch prey.
  • Long-term planning and memory: A squirrel caches nuts and returns to them after months of experience, which would correspond to keeping billions of visual tokens in context using current techniques.

The core of this argument is that it is manifestly viable to do better along multiple axes, including sample efficiency and the ability to perform complex tasks requiring memory. All these examples highlight advanced capabilities that can be achieved at scales well below what is required by existing transformer architectures and training methodologies (in terms of either data or compute). This is in no way meant as an attack on transformer architectures; they are a highly disruptive technology, accomplishing what other types of architectures have not, and they will likely serve as a foundation for further advances. However, there is much more to do.

Next, we delve into each of the examples above in greater detail.

Sample complexity: The language learning efficiency gap

The sample efficiency gap is perhaps best illustrated by considering the core problem of language modeling where a transformer is trained to learn language. A human baby starts with no appreciable language but learns it well before adulthood. Reading at 300 words per second with 1.3 tokens/word on average implies 6.5 tokens/second. Speaking is typically about half of reading speed, implying three tokens per second. Sleeping and many other daily activities of course involve no tokens per second. Overall, one language token per second is a reasonable rough estimate of what a child observes. At this rate, 31 years must pass before they observe a billion tokens. Yet speculations about GPT-4 suggest four orders of magnitude more than a human observes in the process of learning. Closing this language learning efficiency gap (or more generally, sample efficiency gap) can have significant impact at multiple scales:

  • Large models: Organizations have already scraped most of the internet and exhausted natural sources for high-quality tokens (e.g., arXiv, Wikipedia). To continue improving the largest models, better sample efficiency may be required.
  • Small models: In spite of significant advances, further improvements to sample efficiency may be required if we want small language models (e.g., at the 3B scale) to reach the same level of performance as frontier models like GPT-4.

There are common arguments against the existence of a language efficiency gap which appear unconvincing.

Maybe a better choice of tokens is all you need?

This can’t be entirely ruled out, but the Phi series was an effort in this direction with the latest model trained on 10T tokens, implying there’s still a four-orders-of-magnitude efficiency gap between a human and a model which is still generally weaker than GPT-4 along most axes. It is possible that more sophisticated interactive data collection approaches could help close this gap, but this is largely unexplored.

Maybe language learning is evolutionary?

The chimpanzee-human split is estimated to have occurred between 5M and 13M years ago, resulting in a 35 million base-pair difference. The timeline for the appearance of language is estimated to have occurred between 2.5M and 150K years ago. Estimating divergence at 10M years ago and language occurring 1M years ago, with a stable rate of evolution on both sides. This suggests a crude upper bound of 35M/10/2 = 1.75M base pairs (or, around 3.5M bits) on the number of DNA bits encoding language inheritance. That’s around 5 orders of magnitude less than the number of parameters in a modern LLM, so this is not a viable explanation for the language efficiency gap.

On the other hand, it could be the case that the evolutionary lineage of humans evolved most language precursors long before actual language. The human genome has about 3.1B base pairs, with about one-third of proteins primarily expressed in the brain. Using an estimate of 1B base pairs (around 2B bits) that are brain related. This is still around two orders of magnitude smaller than the LLMs in use today, so it’s not a viable explanation for the language learning efficiency gap. It is plausible that the structure of neurons in a human brain, which strongly favors sparse connections over the dense connections favored by a GPU, are advantageous for learning purposes.

Maybe human language learning is accelerated by multimodality?

Humans benefit from a rich sensory world, notably through visual perception, which extends far beyond language. Estimating a “token count” for this additional information is difficult, however. For example, if someone is reading a book at 6.5 tokens per second, are they benefiting from all the extra sensory information? A recent paper puts the rate at which information is consciously processed in a human brain at effectively 10 bits/second which is only modestly more than the cross entropy of a language model. More generously, we could work from the common saying that “a picture is worth a thousand words” which is not radically different from techniques for encoding images into transformers. Using this, we could estimate that extra modalities increase the number of tokens by three orders of magnitude, resulting in 1T tokens observed by age 31. Given this, there is still an order-of-magnitude learning efficiency gap between humans and language models of the same class as GPT-4.

Maybe the learning efficiency gap does not matter?

In some domains, it may be possible to overcome the inefficiencies of a learning architecture by simply gathering more and more data as needed. At a scientific level, this is not a compelling argument, since understanding the fundamental limits of what is possible is the core purpose of science. Hence, this is a business argument, which may indeed be valid in some cases. A business response is that learning efficiency matters in domains where it is difficult or impossible to collect sufficient data: think of robot demonstrations, personalizing models, problems with long range structure, a universal translator encountering a new language, and so on. In addition, improving learning efficiency may lead to improvement in other forms of efficiency (e.g., memory and compute) via architectural improvements.

Model size: The representational efficiency gap

A second direction in which transformer-based models can be improved lies in model size, or representational efficiency. This is perhaps best illustrated by considering the problem of designing models or agents capable of physical or animal-like intelligence. This includes capabilities like 1) understanding one’s environment (perception); 2) moving oneself around (locomotion); and 3) planning to reach goals or accomplish basic tasks (e.g., navigation and manipulation). Naturally, this is very relevant if our goal is to build foundation models for embodied decision making.

The Portia spider has a brain one million times smaller than that of a human, yet it is observed to plan a course of action and execute it successfully over durations as long as an hour. Stated another way, it is possible to engage in significant physical intelligence behavior with 100M floats representing the neural connections and a modest gigaflop CPU capable of executing them in real time. This provides a strong case that much animal intelligence can be radically more representationally efficient than what has been observed in lingual domains, or yet implemented in software. A concrete question along these lines is:

Can we design a model with 100M floats that can effectively navigate and accomplish physical-intelligence tasks in the real world?

It is not clear whether there is an existing model of any size that can effectively do this. The most famous examples in this direction are game agents, which only function in relatively simple environments.

Are transformer models for language representationally inefficient?

While the discussion above concerns representational efficiency for physical intelligence, it is also interesting to consider representational efficiency for language. That is, are existing language models representationally efficient, or can similar capabilities be achieved with substantially smaller models? On the one hand, it is possible that language is an inherently complex process to both produce and understand. On the other hand, it might be possible to represent human level language in a radically more size-efficient manner, as in the case of physical intelligence.

To this end, one interesting example is given by Alex, a grey parrot that managed to learn and meaningfully use a modest vocabulary with a brain one-hundredth the size of a human brain by weight. If we accept the computational model of a neuron as a nonlinearity on a linear integration, Alex might have 1B neurons operating at 1T flops. Given Alex’s limited language ability, this isn’t constraining enough to decisively argue that language models that are substantially smaller than current models can be achieved. At the same time, it is plausible that most of Alex’s brain was not devoted to human language, offering some hope.

The long-term memory and planning gap

A third direction concerns developing models and agents suitable for domains that involve complex long-term interactions, which may necessitate the following capabilities:

Memory: Effectively summarizing the history of interaction into a succinct representation and using it in context.

Planning: Choosing the next actions or tokens deliberately to achieve a long range goal.

Recent advances like O1 and R1 handle relatively short range planning but are significant advancements in this vein. Existing applications of transformer language models largely avoid long-term interactions, since they can deviate from instructions. To highlight why we might expect to improve this situation, note that humans manage to engage in coherent plans over years-long timescales. Human-level intelligence isn’t required for this, though, as many animals exhibit behaviors that require long-timescale memory and planning. For example, a squirrel with a brain less than one-hundredth the size of a human brain stores food and reliably comes back to it after months of experience. Restated in a transformer-relevant way, a squirrel can experience billions of intervening (and potentially distracting) visual tokens before recalling the location of a cache of food and returning to it. How can we develop competitive models and agents with this capability?

Does it matter?

A common approach to circumvent memory and planning limitations of existing models is to create an outer-level executor that uses the LLM as a subroutine, combined with other tools for memory or planning systems. These approaches tacitly acknowledges the limits of current architectures by offering an alternative solution. Historically, as for machine vision or speech recognition, it has always been more difficult to create a learning system that accomplishes the task of interest with end-to-end training, but it was worthwhile when done as the results were superior. This pattern may repeat for long-term memory and planning, yielding better solutions.

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An AI Miracle Malcontent

The stark success of OpenAI’s GPT4 model surprised me shifting my view from “really good autocomplete” (roughly inline with intuitions here) to a dialog agent exhibiting a significant scope of reasoning and intelligence. Some of the MSR folks did a fairly thorough study of capabilities which seems like a good reference. I think of GPT4 as an artificial savant: super-John capable in some language-centric tasks like style and summarization with impressive yet more limited abilities in other domains like spatial and reasoning intelligence.

And yet, I’m unhappy with mere acceptance because there is a feeling that a miracle happened. How is this not a miracle, at least with hindsight? And given this, it’s not surprising to see folks thinking about more miracles. The difficulty with miracle thinking is that it has no structure upon which to reason for anticipation of the future, prepare for it, and act rationally. Given that, I wanted to lay out my view in some detail and attempt to understand enough to de-miracle what’s happening and what may come next.

Deconstructing The Autocomplete to Dialog Miracle
One of the ironies of the current situation is that an organization called “OpenAI” created AI and isn’t really open about how they did it. That’s an interesting statement about economic incentives and focus. Nevertheless, back when they were publishing, the Instruct GPT paper suggested something interesting: that reinforcement learning on a generative model substrate was remarkably effective—good for 2 to 3 orders of magnitude improvement in the quality of response with a tiny (in comparison to language sources for next word prediction) amount of reinforcement learning. My best guess is that this was the first combination of 3 vital ingredients.

  1. Learning to predict the next word based on vast amounts of language data from the internet. I have no idea how much, but wouldn’t be surprised if it’s a million lifetimes of reading generated by a billion people. That’s a vast amount of information there with deeply intermixed details about the world and language.
    1. Why not other objectives? Well, they wanted something simple so they could maximize scaling. There may indeed be room for improvement in choice of objective.
    2. Why language? Language is fairy unique amongst information in that it’s the best expression of conscious thought. There is thought without language (yes, I believe animals think in various ways), but you can’t really do language without thought.
  2. The use of a large deep transformer model (pseudocode here) to absorb all of this information. Large here presumably implies training on many GPUs with both data and model parallelism. I’m sure there are many fine engineering tricks here. I’m unclear on the scale, but expect the answer is more than thousands and less than millions.
    1. Why transformer models? At a functional level, they embed ‘soft attention’ (=ability to look up a value with a key in a gradient friendly way). At an optimization level, they are GPU-friendly.
    2. Why deep? The drive to minimize word prediction error in the context of differentiable depth creates a pressure to develop useful internal abstractions.
  3. Reinforcement learning on a small amount of data which ‘awakens’ a dialog agent. With the right prompt (=prefix language) engineering a vanilla large language model can address many tasks as the information is there, but it’s awkward and clearly not a general purpose dialog agent. At the same time, the learned substrate is an excellent representation upon which to apply RL creating a more active agent while curbing an inherited tendency to mimic internet flamebait.
    1. Why reinforcement learning? One of the oddities of language is that there is more than one way of saying things. Hence, the supervised learning view that there is a right answer and everything else is wrong sets up inherent conflicts in the optimization. Hence, “reinforcement learning from human feedback” pairs inverse reinforcement learning to discover a reward function and basic reinforcement learning to achieve better performance. What’s remarkable about this is that the two-step approach is counter to the information processing inequality.

The overall impression that I’m left with is something like the “ghost of the internet”. If you ask the internet for the answer to a question on the best forum available and get an answer, it might be in the ballpark of as useful and as correct as that which GPT4 provides (notably, in seconds). Peter Lee’s book on the application to medicine is pretty convincing. There are pluses and minuses here—GPT4’s abstraction of language tasks like summarization and style appear super-human, or at least better than I can manage. For commonly discussed content (e.g. medicine) it’s fairly solid, but for less commonly discussed content (say, Battletech fan designs) it becomes sketchy as the internet gives out. There are obviously times when it errs (often egregiously in a fully confident way), but that’s also true in internet forums. I specifically don’t trust GPT4 with math and often find it’s reasoning and abstraction abilities shaky, although it’s deeply impressive that they exist at all. And driving a car is out because it’s a task that you can’t really describe.

What about the future?
There’s been a great deal about the danger of AI discussed recently, and quite a mess of misexpectations about where we are.

  1. Is GPT4 and future variants the answer to [insert intelligence-requiring problem here]? GPT4 seems most interesting as a language intelligence. It’s clearly useful as an advisor or a brainstormer. The meaning of “GPT5” isn’t clear, but I would expect substantial shifts in core algorithms/representations are necessary for mastering other forms of intelligence like memory, skill formation, information gathering, and optimized decision making.
  2. Are generative models the end of consensual reality? Human societies seem to have a systematic weakness in that people often prefer a consistent viewpoint even at the expense of fairly extreme rationalization. That behavior in large language models is just looking at our collective behavior through a mirror. Generative model development (both language and video) do have a real potential to worsen this. I believe we should be making real efforts as a society to harden and defend objective reality in a multiple ways. This is not specifically about AI, but it would address a class of AI-related concerns and improve society generally.
  3. Is AI about to kill everyone? Yudkowski’s editorial gives the impression that a Terminator style apocalypse is just around the corner. I’m skeptical about the short term (the next several years), but the longer term requires thought.
    1. In the short term there are so many limitations of even GPT4 (even though it’s a giant advance) that I both lack the imagination to see a path to “everyone dies” and I expect it would be suicidal for an AI as well. GPT4, as an AI, is using the borrowed intelligence of the internet. Without that source it’s just an amalgamation of parameters of no interesting capabilities.
    2. For the medium term, I think there’s a credible possibility that drone warfare becomes ultralethal inline with this imagined future. You can already see drone warfare in the Ukraine-Russia war significantly increasing the lethality of a battlefield. This requires some significant advances, but nothing seems outlandish. Counterdrone technology development and limits on usage inline with other war machines seems prudent.
    3. For the longer term, Vinge’s classical singularity essay is telling here as he lays out the inevitability of developing intelligence for competitive reasons. Economists are often fond of pointing out how job creation has accompanied previous mechanization induced job losses and yet my daughter points out how we keep increasing the amount of schooling children must absorb to be capable members of society. It’s not hard to imagine a desolation of jobs in a decade or two where AIs can simply handle almost all present-day jobs and most humans can’t skill-up to be economically meaningful. Our society is not prepared for this situation—it seems like a quite serious and possibly inevitable possibility. Positive models for a nearly-fully-automated society are provided by Star Trek and Iain Banks although science fiction is very far from a working proposal for a working society.
    4. I’m skeptical about a Lawnmower Man like scenario where a superintelligence suddenly takes over the world. In essence, cryptographic barriers are plausibly real, even to a superintelligence. As long as that’s so, the thing to watch out for is excessive concentrations of power without oversight. We already have a functioning notion of super-human intelligence in organizational intelligence and are familiar with techniques for restraining organizational intelligence into useful-for-society channels. Starting with this and improving seems reasonable.
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ICML 2021 Invited Speakers — ML for Science

By: Stefanie Jegelka and Ameet Talwalkar (ICML21 Communication Chairs)

With ICML 2021 underway, we wanted to briefly highlight the upcoming invited talks. A general theme of the invited talks this year is “machine learning for science.” The Program Chairs (Marina Meila and Tong Zhang) have invited world-renowned scientists from various disciplines to discuss their problems and the corresponding machine learning challenges. By exposing the machine learning community to these fascinating problems, we hope that we can help to further expand the applicability of machine learning to a wide range of scientific domains. 

  • Daphne Koller (Tuesday, July 20th at 8am PDT): Dr. Koller is a pioneer in the field of machine learning, and is currently the Founder and CEO of Insitro, which leverages machine learning for drug discovery. She was the Rajeev Motwani Professor of Computer Science at Stanford University, where she served on the faculty for 18 years. She was the co-founder, co-CEO and President of Coursera, and the Chief Computing Officer of Calico, an Alphabet company in the healthcare space. She received the MacArthur Foundation Fellowship in 2004, was awarded the ACM Prize in Computing in 2008, and was recognized as one of TIME Magazine’s 100 most influential people in 2012.
  • Xiao Cunde and Dahe Qin (Tuesday, July 20th at 8pm PDT): Dr. Cunde is a glaciologist and Deputy Director of the Institute of the Climate System, Chinese Academy of Meteorological Sciences. He has worked in the fields of polar glaciology and meteorology since 1997. His major research focus has been ice core studies relating to paleo-climate and paleo-environment, and present day cold region meteorological and glaciological processes that impact environmental and climatic changes. Dr. Qin is the Former Director of the China Meteorological Administration. He is a glaciologist and the first Chinese ever to cross the South Pole. He was a member of the 1989 International Cross South Pole Expedition and has published numerous ground-breaking articles, using evidence gathered from his Antarctic expeditions.
  • Esther Duflo (Wednesday, July 21st at 8am PDT): Dr. Duflo is the Abdul Latif Jameel Professor of Poverty Alleviation and Development Economics in the Department of Economics at MIT and a co-founder and co-director of the Abdul Latif Jameel Poverty Action Lab (J-PAL). In her research, she seeks to understand the economic lives of the poor, with the aim to help design and evaluate social policies. She has worked on health, education, financial inclusion, environment and governance. In 2019, she received a Nobel Prize in Economic Sciences “for their experimental approach to alleviating global poverty”. In particular, she and co-authors have introduced a new approach to obtaining reliable answers about the best ways to fight global poverty.
  • Edward Chang (Wednesday, July 21st at 8pm PDT): Dr. Chang is a Professor in the Department of Neurological Surgery at the UCSF Weill Institute for Neurosciences. He is a neurosurgeon and uses machine learning to understand brain functions. His research focuses on the brain mechanisms for speech, movement and human emotion. He co-directs the Center for Neural Engineering and Prostheses, a collaborative enterprise of UCSF and UC Berkeley. The center brings together experts in engineering, neurology and neurosurgery to develop state-of-the-art biomedical technology to restore function for patients with neurological disabilities such as paralysis and speech disorders.
  • Cecilia Clementi (Thursday, July 22nd at 8am PDT):  Dr. Clementi is a Professor of Chemistry, and Chemical and Biomolecular Engineering, and Senior Scientist in the Center for Theoretical Biological Physics at Rice University, and an Einstein Fellow at FU Berlin. She researches strategies to study complex biophysical processes on long timescales, and she is an expert in the simulation of biomolecules using large-scale ML. Her group designs multiscale models, adaptive sampling approaches, and data analysis tools, and uses both data-driven methods and theoretical formulations.

To register for the conference and check out these talks, please visit: https://icml.cc/.

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ALT Highlights – An Interview with Joelle Pineau

Welcome to ALT Highlights, a series of blog posts spotlighting various happenings at the recent conference ALT 2021, including plenary talks, tutorials, trends in learning theory, and more! To reach a broad audience, the series will be disseminated as guest posts on different blogs in machine learning and theoretical computer science. John has been kind enough to host the first post in the series. This initiative is organized by the Learning Theory Alliance, and overseen by Gautam Kamath. All posts in ALT Highlights are indexed on the official Learning Theory Alliance blog.

The first post is an interview with Joelle Pineau, by Michal Moshkovitz and Keziah Naggita.

We would like you to meet Dr. Joelle Pineau, an astounding leader in AI, based in Montreal, Canada.

Name: Joelle Pineau

Institutions: Joelle Pineau is a faculty member at Mila and an Associate Professor and William Dawson Scholar at the School of Computer Science at McGill University, where she co-directs the Reasoning and Learning Lab. She is a senior fellow of the Canadian Institute for Advanced Research (CIFAR), a co-managing director of Facebook AI Research, and the Montreal, Canada lab director. Learn more information about  Joelle here and her talk here.

Reinforcement Learning (RL)

How and why did you choose to work in reinforcement learning?   What are the things that inspired you to choose health as a domain of application for your RL work?

I started working in reinforcement learning at the beginning of my PhD  in robotics at CMU.  Quite honestly, I was delighted by the elegance of  the mathematical formulation.  It also had some link to topics I studied previously (in supervised learning & in operations search).   It was also useful for decision-making, which was complementary to state tracking & prediction, which was the topic studied by many other members of my lab at the time.

I started working on applications to health-care early in my career as a faculty at McGill.  I was curious to explore practical applications, and found some colleagues in health-care who had some interesting decision-making problems with the right characteristics.

How would you recommend a newcomer enter the RL field?  For RL researchers interested in safety, is there some literature you can recommend as a starting point?

Get familiar with the basic mathematical formalism & algorithm, try your hand at easy simulation cases.  For RL and safety, the literature is very small and quite recent, so it’s easy enough to get started.  Work on Constrained MDPs (Altman, 1999) is a good starting point.  See also the work on Seldonian RL, by Phil Tomas and colleagues.

In your talk you mentioned applications of RL to different domains. What do you think is the main achievement of RL? 

The AlphaGo result was very impressive!  Recently, the work on using RL to control the flight of the Loon balloons is also quite impressive.

What are the big open problems in RL? 

Efficient exploration continues to be a major challenge.  Stability of learning, even when the data is non-stationary (e.g. due to policy change), is also very important to address.  In my talk I also highlighted the importance of development methods for RL with responsible properties (safety, security, transparency, etc.) as a major open problem.

Collaborations

Based on your work in neurostimulation, it appears that people from different fields of expertise were involved. 

Yes, this was a close collaboration between researchers in CS (my own lab) and researchers in neuroscience, with expertise in electrophysiology.

What advice would you give researchers in finding interdisciplinary collaborators?

This collaboration was literally started by me picking up the phone and calling a colleague in neuroscience to propose the project.  I then wrote a grant proposal and obtained funding to start the project.  More generally, these days it’s actually very easy for researchers in machine learning to find interdisciplinary collaborators.  Giving talks, offering office hours, speaking to colleagues you meet in random events – I’ve had literally dozens of projects proposed to me in the last few years, from all sorts of disciplines.

What are some of the best ways to foster successful collaborations tackling work cutting across multiple disciplines?

Spend time understanding the problems from the point of view of your collaborator, and commit to solving *that* problem.  Don’t walk in with  your own hammer (or pre-selected set of techniques), and expect to find a problem to show-off your techniques. Genuine curiosity about the other field is very valuable!  Don’t hesitate to read the literature – don’t expect your collaborator to share all the needed knowledge.  Co-supervising a student together is also often an effective way of working closely together.

Academia, industry and everything in between 

During the talk, you mentioned variance in freedom of research for theoreticians in industry versus academia. Could you elaborate more about this? Are there certain personality traits or characteristics more likely to make someone more successful in academia versus industry?

For certain more theoretical work, it can be a long time until the impact and value of the work is realized.  This is perhaps harder to support in industry, which is better suited to appreciated shorter-term impact.  Another big difference is that in Academia, professors work closely with students and junior researchers, and should expect to dedicate a good amount of time and energy to training & developing them (even if it means the work might move along a bit slower).  In industry, a researcher will most often work with more senior researchers, and the project is likely to move along faster (also because no one is taking or teaching courses).

How do you balance leadership, for example, at FAIR, with students advising like at McGill, research [CIFAIR, FAIR, McGill, Mila], and personal life? 

It’s useful to have clarity about your priorities.  Don’t let other people dictate what these are – you should decide for yourself.  And then spend your time according to this.  I enjoy my work at FAIR a lot, I also really enjoy spending time with my grad students at McGill/Mila, and of course I really enjoy time with my family & friends.  So I try to keep a good balance between all of this. I also try to be clear & transparent with other people about my availability & priorities, so they can plan accordingly.

What do you think distinguishes the mindset of an extraordinary researcher?

To be a strong researcher, it helps to be very curious, genuinely want to understand and find out new knowledge. The ability to find new connections between ideas, concepts, is also useful.  For scientific research, you also need discipline and good methodology, and a commitment to deep understanding (rather than “proving” whatever hypothesis you hold).   Frankly, I also don’t think we need to further cultivate the myth of the “extraordinary researcher”.  Research is primarily a collective institution, where many people contribute, in ways small and big, and it is through this collective work that we achieve big discoveries and breakthroughs!

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What is the Right Response to Employer Misbehavior in Research?

I enjoyed my conversations with Timnit when she was in the MSR-NYC lab, so her situation has been on my mind throughout NeurIPS.

Piecing together what happened second-hand is always tricky, but Jeff Dean’s account and Timnit’s agree on a basic outline. Timnit and others wrote a paper for FAccT which was approved for submission by the normal internal review process, then later unapproved. Timnit threatened to leave unless various details about this unapproval were clarified. Google then declared her resigned.

The definition of resign makes it clear an employee does it, not an employer. Since that apparently never happened, this is a mischaracterized firing. It also seems quite credible that the unapproval process was highly unusual based on various reactions I’ve seen and my personal expectations of what researchers would typically tolerate.

This frankly looks bad to me and quite a number of other people. Aside from the plain facts, this is also consistent with racism and/or sexism given the roles of those involved. Google itself now faces a substantial rebellion amongst employees.

However, I worry about consequences to some of these reactions.

  1. Some people suggest not reviewing papers from Google-based researchers. As a personal decision, this is making a program chair’s difficult job harder. As a communal decision, this would devastate the community since a substantial fraction are employed at Google. These people did not make this decision and many actively support Timnit there (at some risk to their job) so a mass-punishment approach seems deeply counterproductive.
  2. Others have suggested that Google should not be a sponsor at major machine learning conferences. Since all of these are run as nonprofits, the lost grants will either be made up by increasing costs for everyone or reducing grants to students and diversity sponsorship. Reduced grants in particular seem deeply counterproductive.
  3. Some have suggested that all industry research in general is bad. Industrial research varies substantially from place to place, perhaps much more so than in academia. As an example, Microsoft Research has no similar internal review process for publications. Overall, the stereotyping inherent in this view makes me uncomfortable and there are some real advantages to working in industry in terms of ability to concentrate on research or effecting real change.

It’s critical to understand that the strength of the research community is incredibly valuable to the community. It’s not hard to imagine a different arrangement where all industrial research is proprietary, with only a few major companies operating competitive internal research teams. This sort of structure exists in some other fields, often to the detriment of anyone other than a major company. Researchers at those companies can’t as easily switch jobs and researchers outside of those companies may lack the context to even contribute to the state of the art. The field itself progresses slower and in a more secretive way due to lack of sharing. Anticommunal acts based on mass ostracization or abandonment could shift our structure from the current relatively happy equilibrium where people from all over can participate, learn, and contribute towards a much worse situation.

This is not to say that there are no consequences. The substantial natural consequences of a significant moral-impacting event will play out regardless of anything else. The marketplace for top researchers is quite competitive so for many of them uncertainty about the feasibility of publication, the disposition and competence of senior leadership, or constraints on topics tips the balance towards other offers. That may be severe this year, since this all blew up as the recruiting season was launching and I expect it to last over many years unless some significant action is taken. In this sense, I expect all the competitors may be looking forward to recruiting more than they were previously and the cost of not resolving the conflict here in a better way may be much, much higher than just about any other course of action. This is not particularly hypothetical—I saw it play out over the years after the silicon valley lab was cut as the brain drain of other great researchers in competitive areas was severe for several years afterwards.

I don’t think a general answer to the starting question is possible, since it will always depend on circumstances. Even this instance is complex with actions that could cause unintuitive adverse impacts on unanticipated parts of our community or damage the community as a whole. I personally hope that the considerable natural consequences here form a substantial deterrent to misbehavior in the long term. Please think this through when considering your actions here.

Edits: tweaked conclusion wording a bit with advice from reshamas.