A number of years ago, I asked myself what would happen if we launched mirrors far into space: could we shine light at them and store data in the photons traveling in the vacuum, preserved and untouchable until the light eventually bounces back at us, potentially centuries into the future?

The idea never left me, but I didn’t have the mathematical tools back then to find out whether the scheme could actually work.

So I did what was accessible at the time: I wrote a short story around the idea, unburdened by physics and reality. Still, it is one thing to write pure fiction, but it’s another altogether to publish a story that is so close to actually plausible physics without knowing whether it all adds up. It felt like lying. And thus I tabled it until I could get better answers.

Until today! I now have at my fingertips the AI tools to answer the questions that had stumped me for so long. I am still no closer to being an expert in relativistic physics, but at least I have one informed opinion to lean on. My AI expert confirms what I suspected: the math doesn’t entirely add up. But knowing this, and being able to share the analysis, I don’t have to feel too bad about misleading my readers and projecting them into an alternate universe that is close to ours, but where echoes from the past shine back at us from deep space.

The result: a new experimental sci-fi mashup of sorts. On one hand, a 100% human-written short story of grief and civilization collapse. On the other, a purely AI produced exploration of the physics underlying the story.

Interactive site: https://vvanhoucke.github.io/light/

Enjoy!

I remember vividly the day my research career could have ended before it even started. I was sitting on a couch at a conference next to Prof. Mark Gales, from Cambridge University, when he turned to me and asked: ‘so, what are you doing your thesis on?’

Here it was … the only ‘thesis defense’ that really mattered in the speech recognition community. Mark’s research taste was widely acknowledged, and approval from him meant a lot. He was notorious for walking around poster sessions at conferences and tearing apart people’s arguments, in that ever so understated, humorous way that made it sting twice as much. He usually attracted a crowd. I was glad at that moment that my roasting was going to happen in private, and before I had started committing significant time to my research.

And a proper roast it was. One that lasted a whole 5 minutes, because Mark immediately got what I was trying to do, and immediately dismantled its very premise. It wasn’t a terrible idea, it would probably work. It just didn’t matter. Without going into details, my plan was to come up with better estimates of parameters that, it turned out, had next to no impact on actual outcomes when you got them slightly wrong. Perhaps I would have eventually gotten to that realization, but this was my first taste of how easy it can be to fall for an idea that addresses the wrong question, and how important developing a taste for what problems are worth solving was.

This is not merely an issue for individual researchers, but is equally relevant for entire fields of research. My favorite example is the state of machine learning theory in the 2010s. Much of ML theory then was about characterizing the generalization gap:

Many ML practitioners were puzzled by this however: the world we were all living in since the advent of Deep Learning looked more like the picture below, with huge, overparametrized models that seemingly defied all theory:

It took another decade before the double descent phenomenon was characterized, a decade spent mostly trading ‘you’re doing it wrong’ accusations between theorists and practitioners. This video does an excellent job at illustrating this longstanding disconnect. It was very clear, at least to some of us, that a form of collective streetlight effect was at play, and that much of ML theory research produced in that period was never going to inform practice or have any durable impact.

Picture a world where we collectively, theorists and practitioners, embraced the oddity of large deep networks and made them the focus of study earlier. My bet is that neural scaling laws would have emerged from that inquiry much sooner, and shaped our design choices at a much earlier stage in the pre-Transformer era. That opportunity cost alone is likely measured in years of global progress.

To be fair, ML practitioners had been suffering from a similar blindness, in the form of going after pretty maths and algorithmic complexity over data scalability. In the heyday of factor analysis and graphical models of all ilks, we’d collectively failed to recognize that compute efficiency and data scaling were absolutely critical in a world where compute and storage were getting cheaper every year. To this day, I am convinced that backpropagation won out because it is fundamentally free of high-polynomial-degree operations such as matrix inversions, SVD, eigenvalue decompositions, or approximations thereof.

This makes me reflect on what kind of precursor signals to look for when picking a research topic, so that it has a chance to make an impact, and maybe survive the test of time?

Looking back, some of the most impactful works I was involved in focussed on simple, overlooked truths. I have been co-author on two ‘test-of-time award’ papers, but the one paper I’m most proud of, and which has probably had the most durable impact, won’t get an award anytime soon: it was an objectively underbaked paper, with a poorly thought-out baseline, and only barely appropriate as a workshop submission. But it described a simple and powerful idea: you could quantize neural networks down to fixed-point 8-bit operations and not lose performance. The idea wasn’t even entirely novel, since by then Clément Farabet, Eugenio Culurciello, Yann LeCun and others had already taken advantage of heavy quantization in their neural hardware accelerators. But the idea that this was useful in software wasn’t out there, and the area of low-precision neural network research had yet to flourish. I hope that this paper had a modest hand in making it happen. For us at Google, it had immediately unlocked our ability to deploy a deep-learning powered Voice Search at scale (back in 2011, before wide adoption of GPUs,) possibly the first deep learning system to be deployed in production at such scale at the time.

Another paper in the same vein of exposing the world to underappreciated concepts was a study that showed how rectified linear units (ReLU) were a terrific idea, even if you were not doing computer vision or sparse coding. Again, we were hardly the first to use ReLU, but it had yet to become the mainstream staple of deep networks it is today.

In contrast, my biggest academic regret is not having sufficiently pestered Laurent Sifre, who was interning with me at the time, to fully describe one such ‘simple idea’: separable convolutions, in a standalone paper. He had described it in a dark corner of his thesis, and I had mentioned it in a talk. We used it in Inception v3. But it took another 3 years for it to be described as a standalone concept by François Chollet, who did an excellent extensive analysis of the concept. Its very simplicity blinded us to its broad relevance to neural network architecture design.

Simplicity is not always a gift. A good way to not have impact is to take the next ‘simple’ logical step in an existing line of research. My own PhD thesis was an example of a ‘barely worth it’ piece of research: on the surface, it was a respectable 6x improvement in speed for a certain class of models, or a 15% in accuracy depending on where you lived on the Pareto frontier. But it improved incrementally, and in a rather straightforward manner, upon someone else’s research. Not in such an original way that that same group didn’t come up with a very similar scheme. My research made it into production, I got a doctorate out of it, and learned a few lessons along the way, but I would not call this work high academic return on time spent. It didn’t do much to move science forward, and ended up being largely duplicative.

It’s also important to question how quickly any given research is likely to be obsolete in the best case scenario. This is often a problem for research that aims to improve the system characteristics of an algorithm like speed, latency or memory use: you are racing against a moving target, Moore’s law, Kryder’s law, or their modern equivalents. You only have an impact if you’re effectively and durably removing an active constraint on the system that is independent of the hardware’s progress.

Predicting these kinds of computing trends is hard. Our early work on neural network quantization continues to get to the heart of one of today’s active constraints of memory bandwidth and capacity, but it was not a given at the time. It is a little easier for systems research today because, to a first order approximation, we are all basically bottlenecked on thermodynamic limits: if you can translate your systems research into picojoules, you can evaluate how large a dent you can make into the total power envelope of the system, and this improvement has a high likelihood of being durable. It does make one wonder where all the neuromorphic hardware efforts, which were loudly marketing low-power designs for decades, have all gone, now that FLOPS / W is finally the active constraint in AI.

One consideration is whether your research is itself anchored in time, or timeless by design: are you relying on assumptions that are true today, but are likely to change as technology and humanity progress? For instance, there is a class of research that is obsolete almost the minute it is produced, and yet remains astonishingly popular. To pick an example from my own portfolio, my very first paper was about looking at how people interacted with search by voice. This was descriptive research: taking a system — here the user and a search engine — and observing it, trying to draw broader conclusions. The pitfall is doing descriptive research on something that itself is evolving: I am pretty sure that any finding from my search study has long been invalidated, because the system itself that was being studied has changed dramatically over the years, both the technology and people’s expectations of it. In fact, looking back, whether the study generalized beyond the very setup we employed is dubious at best. In contrast, there is a lot of value in descriptive research if the system you’re studying is part of nature (e.g., botany), the historical record, or universal laws (e.g., mathematics.) These subjects of descriptive study generally have in common that the topic of study is a stable aspect of the world, suitable for drawing durable inferences. But when your subject is something as fleeting as people’s relationship with technology, there are infinitely many such systems to study, and infinitely many ways to collect data and produce results, all anchored in how we relate to technology at this specific moment. This is my main issue with a large swath of human factor research: descriptive experiments that are very dependent on the setup, time, and place, and pay lip service to the idea that they’re uncovering more fundamental truths about how humans and machines interact, without spending commensurate effort towards actually establishing their degree of generalization.

Another question to ask is whether you’re attacking the core of the problem, or something peripheral to it. To borrow an example from my years of working on speech recognition: many researchers used to go after the side quest of ‘what to do when speech recognition fails?’, instead of addressing the core issue of improving its success rate. Error recovery was a significant chunk of every ICASSP conference. But none of that literature has had any durable impact as systems kept improving. I see the same pattern developing in robotics today: research of the form ‘assume your robot is as clumsy as the state of the art today: how do we compensate for it?’ Little of that research is likely to ever matter either as systems continuously get better.

Another potential trap is working on a narrow, targeted subset of a broader problem, when the broad problem itself is unsolved. This one is somewhat subtle, but let’s again turn to speech recognition as an example: speech conferences used to be littered with papers on improving performance for far-field speech, noisy speech, accented speech, low-resource spoken languages, children’s speech, etc, … Now that the dust has settled a bit, one can broadly say that little from this class of research has had any lasting impact on the field: the problem was not about solving speech recognition for X, it was about solving speech recognition period. It turns out that improving the system for the head and torso of the distribution had a disproportionate impact on the tail. Generally speaking, many of the more targeted improvements were washed away by improvements to the more general system.

This is a common pattern whereby the symptom is failure at the edges of the distribution, while the cause is a weakness at the core: a poor speech recognition system may manifest itself as not working well in noisy conditions, but the solution itself may not have anything to do with noise. I see this at play in autonomous driving today: many of the long-tail issues we observe don’t get addressed by solving ‘for the tail’: they make us reconsider core system assumptions that have broad impact on every quantile of the distribution.

A similar dynamic can be observed in language modeling, where improving core LLMs has wiped away the impact of many fields of research that attempted to solve for what was fundamentally a slightly reframed language modeling problem (e.g. topic modeling, summarization, information retrieval…) To be clear, I am not arguing to not work on niche problems as a way to derive new insights: ‘Attention is all you need’ was a machine translation paper in the first place, and drew insights from the sentence reordering problem which ended up revolutionizing NLP at large. But it is important to make sure that the assumptions made in a specific context do not box you into the narrow subject matter, and help inform the broader question.

I hope that I’m conveying here that my goal is not to throw shade at specific areas of research, but rather to look at patterns of durable impact:

• Consider impact from the beginning: you don’t need to have a solution to get a sense of whether a problem is worth solving,
• Consider the competitive landscape: I love to tell people that if you’re worried about being scooped, you’re probably working on the wrong problem. An obvious follow-up of an existing paper is likely to attract a crowd,
• Mine your research for simple, overlooked ideas: if in the course of researching something else you stumble on such a nugget, consider whether to pivot to investigating that more deeply, leveraging your intended research as supporting evidence,
• Look for truths that are stable over time: conditioning the success of your research on the overall state of the world remaining unchanged is a sure way to be obsolete from the start. This is incidentally what makes doing AI research so difficult today: findings that are tightly dependent on the performance of current foundation models are essentially noise,
• Attack a core problem of your field: research on ‘meta’ problems or problems that are adjacent to core issues tend to have less durable impact,
• Love the problem, not the solution: ugly solutions to important problems are valuable precisely because they are less likely to get attention, and shed light on our collective biases.

Many of these considerations may sound trivial, if not for the fact that I can point back to very concrete examples in my career where I strayed from them, at a personal opportunity cost that is probably measured in years of work. Admittedly, this overlooks the fact that I would probably not have been on the same learning journey if I had not stumbled on those pitfalls along the way.

As for the papers that did get recognized with prizes and awards, they all have in common this one final piece of advice: surround yourself with very smart people, recognize when they have brilliant ideas, and be ready to roll up your sleeves and make their work shine brighter.

I am occasionally asked to consult on AI projects by friends or colleagues. Since I will admit I do not always love this kind of engagement, I have developed a surefire “fail fast” response, which has the dual benefit of actually providing them with immediate actionable advice, while ensuring that most will never talk to me about AI ever again.

It often begins with: “So … I have this machine learning problem.”

This is when I strike the iron while it’s hot. I channel my best Alex Trebek (it gets easier as years go by) and ask:

“Please state your problem in the form of an eval.”

What is an “eval”? It’s two things. First, a test set, a representative set of about 1,000 inputs (more on this figure later) to your system that you want to apply learning methods to, each annotated with the desired outputs. Second, a measure of success, which for any given input in your eval, gives you a figure of merit for any proposed output, possibly by comparing it to the desired output you have annotated.

That’s it. That’s the whole conversation. And it is, shockingly, probably the only conversation that anyone who wants to use AI needs to have.

Producing an eval is both a necessary and sufficient condition to use AI to solve your problem, or finding out quickly that it can not be solved.

Let’s unpack.

First of all, 90% of the conversations will stop there, simply because people will fail to produce said eval. It may be that the problem they have is not “AI shaped.” Or not well-defined, in which case sharpening the problem specification needs to happen first. Or maybe they merely say they care about solving the problem, but just not enough to actually produce an eval.

This is why I start with this 1,000 figure for the required number of inputs: it’s near the lower threshold of producing statistically significant “round” accuracy numbers like 88%, assuming binary classification. It is also sufficient “proof of work” to demonstrate that the problem is worth solving: a good use of my time, and of AI automation in general. Obviously, that figure can be relaxed depending on the actual problem at hand.

Notice that I have made no mention of “how” to actually solve the problem — no talk of models, technologies, algorithms, or even training data. I claim instead that having an eval is sufficient for either solving your problem with AI, or finding out that no such solution is available. The “how,” it turns out, is generally the easy part.

Simply put, evals are catnip for ML engineers.

ML engineers can’t resist a good metric: once it’s there in front of their nose, it’s got to go up, at any cost. Put yourself into their shoes: for their entire career, product managers have come to them with ill-posed problems, of dubious relevance, with no data, and no measure of success. They typically have to do the work of building an eval from scraps of requirements and SQL queries into the darkest recesses of their BI system. They hate it. This is not the fun part of AI. People with advanced degrees in AI have done their graduate program in a world where all the training sets, test sets, metrics and problems are generally well-defined. The rules are clear, and building a better model is the name of the game. People who build those evals are hailed as heroes of the academic world, with the implied subtext “better them than me …” For many engineers, their first contact with industry is a cold shower, with most of their time spent in data and eval curation. If you, as a problem owner, can lift that burden from their shoulders and bring them a clear metric to hillclimb, they will love you forever, and more pragmatically, will be much more likely to shower you with results.

Having an eval is also a necessary condition to use AI. At the very minimum, your deployed system will need regression testing, but most likely you will want to hillclimb on eval performance for a while before getting to a good operating point, hence front-loading building said eval comes at no cost to your actual timelines.

This eval-first approach extends to working with vendors. If someone wants to sell you an AI solution, whip out your eval, and you will quickly know if they’re the real thing. Give them half of the data to score themselves, and keep half to cross reference their results. I saved you a sales pitch, and sped up your due diligence by months.

As a litmus test for ML experience, you can generally tell a junior ML engineer from a seasoned one by the way they think: fresh out of grad school, you start with the model, then think about the data, and finally the eval. Seasoned engineers think eval first, data next, and maybe then get to modeling. This is exacerbated by the trend towards zero or few-shot learning, where you may very well find that you never have to worry about the latter two.

There are parallels between this “evaluation-driven ML engineering” and other practices such as “test-driven development,” which I credit for my surviving my first decade of software engineering at Google, as well as OKR culture, which shifts goal-setting from asking “what we’re going to do” to “how will we know we got what we wanted.” Maybe it is time we embrace this methodology in machine learning as well, and, in the process, reaffirm data science as the beating heart of ML engineering. Without it, we are fated to soon become all but “prompt kiddies,” entrusting blindly our outcomes to the vagaries of LLM capabilities.

The AI panic du jour is not about any new doomsday AGI scenario, but about AI progress slowing down too fast. Maybe. Having lived through a few similar bouts of collective, huh, performance anxiety, in domains as varied as speech recognition and computer vision, I thought I’d comment on a few ways one can fool oneself into seeing stagnation everywhere.

Let’s first examine some simple geometric facts. None of this will be new to most of my data scientist colleagues, but it is an issue I often see reflected in popular commentary. Say you’re measuring accuracy on a benchmark. Accuracy is bounded above by 100%. Technology doesn’t regress, so performance over time can only be non-decreasing. Assume that at some point in time, technology is at a certain baseline level. Performance goes up, everybody gets excited:

Consider what can possibly happen next. Even in the best of scenarios, the only shape such curve can take over time, by virtue of being non-decreasing and bounded above, is something like:

However, you often see it depicted like this:

Did I have to make any assumption about technology ‘slowing down’ to plot this curve? No! It’s purely a geometric artifact of focussing on accuracy (or equivalently, error rates) as the metric, and of using a fixed benchmark. A linear or concave curve in such a ‘bounded above’ scenario would mathematically have to be a short-lived exception. What matters to measuring progress is ‘what fraction of the remaining errors do we fix over time.’ A constant rate of progress would be fixing X% of the remaining errors over a given interval.

For instance, picture cutting 10% of the errors in your system at a fixed cadence:

It looks like a slowdown in progress, but the rate of improvement is in fact constant: of all the errors you observe at any given instant in your system, you effectively fix the same fraction of them every time period. It is very unintuitive to think in terms of relative rate of errors, but empirically this is what every benchmark leaderboard looks like. For instance, it takes 22 iterations of a 10% relative improvement to take a system from a 10% error rate down to 1%. You may think of it as a 10x improvement, and it would be right from a user’s standpoint — they encounter an error 10 times less often. But it takes hacking away at 10% of the observed errors more than twice as many times just to get there. It is a slightly different take on the law of diminishing returns: rarer problems take on a larger fraction of the total error budget as the model gets better, and it also often takes proportionally more effort and data to get robust statistics for them.

Empirically, that 22x factor is much more reflective of the actual engineering work involved to get an order of magnitude improvement. Changes to a system, assuming they’re orthogonal to each other, are generally not additive. My 10% improvement and your 10% improvement combined will yield at best a 19% total gain, not 20%, assuming one of us is using the other as their baseline. And independence is a huge assumption in and of itself: typical modeling improvements nibble at errors that are closest to the margin, and generally yield very correlated changes in behavior. This is why the infinite number of PhD theses claiming 10% improvement here, 10% improvement there, even on the latest baseline, appear to never add up to a massive improvement in SOTA.

If you’re curious, it takes 11 sequential 20% improvements, and 7 sequential 30% improvements to improve the system by 10x. Basically, whatever your relative improvement is, think of it as about half as ‘potent’ as the number would naively suggest.

This apparent slowdown is also an artifact of reporting on a fixed dataset. Machine learning has always been a process of co-evolution between benchmarks and technology. As a community, we never really ‘solve’ a benchmark, we merely forget about it and move on to the next one. I am still amazed by the speed at which we collectively ditched the Turing test at the first whiff of it being within reach. I stopped paying attention to the popular CIFAR10 benchmark at a time when performance hovered around 90%. That was when ImageNet became all the rage, and people became much more excited about evaluating their models on more realistic tasks. Recently, I was shocked to realize that today’s performance on CIFAR10 is a staggering 99.5%. That’s 20x better than when I was last losing my hair trying to scrounge 0.1% improvements on it, and I had not even noticed. This self-inflicted amnesia over how far we’ve come at the scale of multiple decades is another way of losing sight of the overall arc of progress.

A similar geometric fallacy can be found when fishing for ‘inflection points.’ With all the exponential curves being tossed around these days, and various flavors of scaling laws in particular, people rightfully want to predict if and when they might end. There is a common saying that ‘every exponential is a sigmoid in disguise’: there is always a ceiling to exponential processes, generally due to physics or the finiteness of resources (even ‘sustainable’ ones, hah.) By the same argument I made above for the existence of a bounded ceiling, a growth curve has to mathematically bend in order to not meet that ceiling (until a breakthrough eventually lifts it):

You often see commentary about predicting the inflection point of this and that exponential curve (predictions around the end of Moore’s law are a typical example.) That is a very valid scientific question to be asking in general.

What makes no sense is trying to predict that inflection point from the curve itself: it is a second order effect, a derivative of a derivative. Whatever granularity you measure the change at, you need to be two steps in the future past the inflection point to even get a single point estimate of that effect, let alone a robust statistic to make any confident prediction about it. Simply put: stop squinting at your log-plot to see if the exponential growth you’re riding is over: in the absence of a model that is extrinsic to the observed data, you can only identify inflection points way after they’ve actually occurred, and definitely past the window of usefulness of such prediction.

Does this say anything about where AI is headed today? Not really. All I am trying to convey is that the very way we report results in AI lends itself to the ‘diminishing returns’ narrative in a way that doesn’t reflect actual progress, and that observing the rate of progress itself is not particularly predictive of anything but the past. Whether we’ve hit an inflection point in scaling laws will only become clear in hindsight. As of today, I’m optimistic, on the basis that we’ve barely even scratched the surface of what real-world data sources can contribute to AI scaling beyond text, even though it is fair to assume that incorporating those efficiently may involve rethinking some aspects of our overall model architecture.

You are today the total sum of all the experiences you have had in your life. They have shaped your identity, your belief system, and your cognitive outlook on the world. What I particularly want to emphasize here is that you have had a singular trajectory through life: one path through time and space that has shaped who you are today. As a consequence, anyone else interacting with you can assume that you have a singular opinion, even if nuanced, about anything of importance: there are foods you like and dislike, perhaps you’re an early riser, or a glass half-full person. You have a unique perspective on the world, and a largely consistent set of beliefs and values. With a few judicious questions, someone can probably get a sense of where you land on the political spectrum, what your religious beliefs are, where your interests lie, and expect them to remain both singular and consistent over time.

LLMs do not have that singular path through life that shapes a unique belief system. In some sense, they have had all the paths through life. They’re a plumber from Alabama, an 18th century poet, a 15 year old Reddit troll, and everyone else that has ever contributed data to the model. They are all these at once, not some average over them. They don’t have one identity, they have all the identities. Not one religion, not one political view, but all the beliefs and values ever expressed on the web. And you can trigger each of these personas by clever prompting: ask a question that would typically raise the interest of one particular group, and the LLM will respond in the voice of that particular internet constituency. Ask a home improvement question, and it’s the web’s DIY hackers responding. Ask about a disease, and you’re likely to get the medical experts (and maybe some hypochondriacs as well.) There isn’t a guarantee that you will consistently elicit a unique voice from the model. It can meander and diverge, which is why prompt injection attacks are often so successful. But to a large extent, this ‘multi-polarity’ is a desirable feature: you want the model to speak in the voice of the expert and give well-informed advice on any topic.

This is not an original idea. Engineers working on this technology have all internalized this concept to some degree. However, many fail to realize that, by and large, the rest of the world has not. A huge problem we face in the public perception of LLMs today lies in the fact that it is extremely challenging for us humans to comprehend that we’re talking to an entity that is not a singular entity, with a unique life experience and set of views.

We talk to a chatbot and expect that the intelligence behind it to have a personality, an association encouraged by the chatbot format. That expectation is so ingrained in the public’s imagination that much of the media chatter around LLMs centers on: this one AI is acting Nazi, or that other AI is “woke.” But the truth is they’re some shade of both, and everything in between. They are not shaped by a unique past.

There is nothing fundamental about intelligence requiring having a unique worldview. Even our attempts at portraying similar swarm intelligence in science fiction fall short: the Borg of Star Trek have their queen, clearly the embodiment of some sort of emergent consistent persona, even when they are meant to be a “collective.” Brandon Sanderson’s “Legion” has its Stephen Leeds, whose personal narrative is the single thread around which all the lives of the several personas that inhabit his brain are woven. We can’t seem to imagine or relate to a distributed intelligence without giving it an identity, even though our experience of LLMs suggest that this may not be a requirement.

What LLM providers attempt to do is make their systems give the feeling of having a consistent identity with pro-social and generally middle-of-the-road values to their users. But much of what they’re actually doing boils down to upweighting the latent personas in the system that correlate with these attributes, thereby fueling the illusion of AIs having an opinion or worldview, without fundamentally changing the fact that this is not possible for this class of AIs.

I find it fascinating how much we humans care and rely on being able to attach such labels to the entities we interact with. LLMs are the first alien intelligence we encounter that is “swarm-like,” made up of a multiplicity of perspectives fused in a way that does not seek consensus, but reflects the diversity of its constituents. It makes me question whether sentience does have such a requirement, as we have never been confronted with a sentient entity that hasn’t had a unique path through life.

More pragmatically, while I understand that much of the work aiming at curbing the personality traits that these models display has immediate functional value in making them safer to use, I increasingly see the problem as having more to do with compensating for our own cognitive flaws. I do wonder how we may be able to achieve similar goals without working against what makes LLMs so rich in their diversity of experiences.

A few months ago, I was faced with a choice: some health issues needed my time and focus, while my work, leading Robotics research at Google DeepMind, demanded increased attention. I made a snap decision: doing both in parallel would ultimately be a disservice to the team and to my own recovery. Stepping back wasn’t a difficult decision: the team at Google DeepMind is absolutely wonderful, and my tech leads in particular were ready to step up to pick up the reins. And so they did, which opened up for me the tantalizing question: after 8 years of taking this effort from zero to what I still humbly consider the best research team on robotics and AI today, what could be next?

Building this team was my third ‘career’ at Alphabet, after working on speech recognition in Android and computer vision on the Brain Team. Through every transition, I’ve sought roles where I can bring 50% of the familiar with me, and 50% learn something new. It was time to take another step into maximizing my impostor syndrome.

While going from medical appointment to physical therapy session, as yet unable to drive myself due to physical limitations, I got to spend a lot of this reflection time inside a Waymo car, clocking dozens of rides all across San Francisco. I can confidently say that I have never interacted with an AI product that is such a delight. Within the first couple of rides, as the novelty inevitably fades, you’re left with a deep sense that this is how personal transport ought to be. The case for this use of AI being of net social benefit was immediately self-evident: it helped me directly in a time of need — I genuinely don’t want to drive a car ever again. I also don’t need to hear another appeal to the inevitability of AGI to make a case for this being the right product/market fit at the right time.

It is not perfect of course, and I find grounds to file user feedback almost every other ride. Which is a good segue into: why work here? I made the case at CoRL last year that too much of robotics research was focused on taking research to the least publishable unit of ~70% performance levels, but not looking as much at the 9X+% problem. I also argued that taking robotic systems to high levels of performance and safety was not about ‘engineering details’ or ‘more data,’ but required different breakthroughs. My first few weeks at Waymo have only reinforced this perspective.

In robotics, autonomous driving included, the long tail of difficulty is increasingly more about common sense reasoning than about low-level planning and control. It is about a deep understanding of the situation and reasoning not just about geometry, but about the semantics of a scene, which in a multi-agent scenario includes other agents’ actions. Much of it is also about scaling: every order of magnitude you grow your usage, every new context you bring your autonomous system into, brings you to the very edge of your generalization capabilities. In that sense, my favorite grand challenges in perception, semantic understanding and reasoning have not aged a bit. But what is different today is that with large multimodal models we have new tools at our disposal to address them.

And it’s not just a theoretical exercise either. These approaches are making it into real deployment today and making a difference. Simply put, there are few places today that can legitimately claim to have connected AI, robotics, and real-world users, and can even start looking at this next generation of technological challenges. Even fewer perhaps that are doing it with such a strong culture of safety at their core, which enables each and every engineer to work knowing that they are backed by the best supporting processes every step of the way. Most ‘AI robotics’ startups and industry efforts are rightfully still focussed on the data problem (I discussed some of the challenges here), but there is something liberating about exploring what happens when data collection is no longer the dominant bottleneck and you’ve already made contact with reality at some scale.

If this sounds like an ad, it kind of is: we’re investing, expanding, and hiring for every ML function, across research, engineering and leadership. Join us! (Opinions remain my own, not that of Waymo.)

Workshops

Agile Robotics: From Perception to Dynamic Action, organized by Huang (Raven) Huang, Shouren Huang, Jeffrey Ichnowski, Atil Iscen, Yuntao Ma, Gabriel Margolis, Pannag Sanketi, Daniel Seita, Guanya Shi, Joanne Truong, Yuji Yamakawa, Yuxiang Yang and Tingnan Zhang.

NEW! Check out our fully open-source Barkour quadruped design.

Mobile Manipulation and Embodied Intelligence (MOMA.v2) — speaker: Keerthana Gopalakrishnan

Vision-Language Models for Navigation and Manipulation, organized by Chris Paxton, Fei Xia, Karmesh Yadav, Nur Muhammad Mahi Shafiullah, Naoki Wake, Weiyu Liu, Yujin Tang adn Zhutian Yang
- Debater: Ted Xiao
- Paper: AutoRT: Embodied Foundation Models for Large Scale Orchestration of Robotic Agents, Michael Ahn, Debidatta Dwibedi, Chelsea Finn, Montserrat Gonzalez Arenas, Keerthana Gopalakrishnan, Karol Hausman, brian ichter, Alex Irpan, Nikhil J Joshi, Ryan Julian, Sean Kirmani, Isabel Leal, Tsang-Wei Edward Lee, Sergey Levine, Yao Lu, sharath maddineni, Kanishka Rao, Dorsa Sadigh, Pannag R Sanketi, Pierre Sermanet, Quan Vuong, Stefan Welker, Fei Xia, Ted Xiao, Peng Xu, Sichun Xu, Zhuo Xu

Advancements in Trajectory Optimization and Model Predictive Control for Legged Systems — speaker: Yuval Tassa

Events

Open X-Embodiment mixer: Wednesday May 15th, 5:45 PM — 6:45 PM

Session Chairs

AI-Enabled Robotics I: Montserrat Gonzalez Arenas

Papers

RoboVQA: Multimodal Long-Horizon Reasoning for Robotics, Pierre Sermanet, Tianli Ding, Jeffrey Zhao, Fei Xia, Debidatta Dwibedi, Keerthana Gopalakrishnan, Christine Chan, Gabriel Dulac-Arnold, Sharath Maddineni, Nikhil J Joshi, Pete Florence, Wei Han, Robert Baruch, Yao Lu, Suvir Mirchandani, Peng Xu, Pannag Sanketi, Karol Hausman, Izhak Shafran, Brian Ichter, Yuan Ca

Decomposing the Generalization Gap in Imitation Learning for Visual Robotic Manipulation, Annie Xie, Lisa Lee, Ted Xiao, Chelsea Finn

How to Prompt Your Robot: A Prompt Book for Manipulation Skills with Code As Policies, Montserrat Gonzalez Arenas, Ted Xiao, Sumeet Singh, Vidhi Jain, Allen Z Ren, Quan Vuong, Jake Varley, Alexander Herzog, Isabel Leal, Sean Kirmani, Dorsa Sadigh, Vikas Sindhwani, Kanishka Rao, Jacky Liang, Andy Zeng

RoboTAP: Tracking Arbitrary Points for Few-Shot Visual Imitation, Mel Vecerik, Carl Doersch, Yi Yang, Todor Davchev, Yusuf Aytar, Guangyao Zhou, Raia Hadsell, Lourdes Agapito, Jon Scholz

Best Paper Award! Open X-Embodiment: Robotic Learning Datasets and RT-X Models, The Open X-Embodiment Collaboration

Best Paper Award in Robot Manipulation! SARA-RT: Scaling up Robotics Transformers with Self-Adaptive Robust Attention, Isabel Leal, Krzysztof Choromanski, Deepali Jain, Avinava Dubey, Jake Varley, Michael Ryoo, Yao Lu, Frederick Liu, Vikas Sindhwani, Quan Vuong, Tamas Sarlos, Ken Oslund, Karol Hausman, Kanishka Rao

Mastering Stacking of Diverse Shapes with Large-Scale Iterative Reinforcement Learning on Real Robots, Thomas Lampe, Abbas Abdolmaleki, Sarah Bechtle, Sandy H. Huang, Jost Tobias Springenberg, Michael Bloesch, Oliver Groth, Roland Hafner, Tim Hertweck, Michael Neunert, Markus Wulfmeier, Jingwei Zhang, Francesco Nori, Nicolas Heess, Martin Riedmiller

Physically Grounded Vision-Language Models for Robotic Manipulation, Jensen Gao, Bidipta Sarkar, Fei Xia, Ted Xiao, Jiajun Wu, Brian Ichter, Anirudha Majumdar, Dorsa Sadigh

Conditionally Combining Robot Skills Using Large Language Models, K.R. Zentner, Ryan Julian, Brian Ichter, Gaurav S. Sukhatme

Distilling and Retrieving Generalizable Knowledge for Robot Manipulation Via Language Corrections, Lihan Zha, Yuchen Cui, Li-Heng Lin, Minae Kwon, Montserrat Gonzalez Arenas, Andy Zeng, Fei Xia, Dorsa Sadigh

Robotic Offline RL from Internet Videos Via Value-Function Learning, Chethan Bhateja, Derek Guo, Dibya Ghosh, Anikait Singh, Manan Tomar, Quan Vuong, Yevgen Chebotar, Sergey Levine, Aviral Kumar

Learning Manipulation of Steep Granular Slopes for Fast Mini Rover Turning, Deniz Kerimoglu, Daniel Soto, Malone Lincoln Hemsley, Joseph Brunner, Sehoon Ha, Tingnan Zhang, Daniel I. Goldman

Robots That Can See: Leveraging Human Pose for Trajectory Prediction, Tim Salzmann, Lewis Chiang, Markus Ryll, Dorsa Sadigh, Carolina Parada, Alex Bewley — Top entry on the JackRabbot Trajectory Forecasting leaderboard

This article is a companion to my upcoming talk at Nvidia GTC, with a sprinkle of spice on top. These are my personal views, not Google DeepMind’s, and don’t necessarily reflect the diversity of perspectives from my team and colleagues.

The buzz at the most recent Conference on Robot Learning, which took place six months ago in Atlanta as of my writing, was noticeably different from any other installment I have attended since its inception seven years ago. There was a sense of change in the air. Many presentations showcased robot systems that actually … kind of worked! Albeit within the confines of certain academic definitions of “working.” Where the community had previously struggled on simple tasks akin to stacking red blocks on top of blue blocks, we were now seeing systems that exhibited real progress on complex, real-world problems.

I often joke that a career in research is about committing to a lifetime of working on things that don’t work. And during hallway conversations between sessions, you could hear researchers asking themselves: “Now what?” — Not because things were actually working well enough that we anyone would call “mission accomplished” on the entire enterprise. Rather, it reflected a realization that the pace of progress in robotics had accelerated, and called for a reevaluation of both the research directions and the methodologies employed.

How did we get there? Well, like all things AI we can trace the shift back to GPT and the dawn of modern LLMs circa 2021. Suddenly, unprecedented reasoning capabilities seemed to be at everyone’s fingertips, and AGI was around the corner. Something else happened to the world of robotics around that time, much less reported in the popular press: massively increased levels of FOMO. Robotics, or “Embodied AI” in its more fashionable garb, was supposed to be the path to AGI, the one true solution to situated intelligence, real-world grounding, and commonsense reasoning. Seeing “Language Modeling,” this obscure subfield that the NLP community had arguably left languishing for a decade, suddenly hogging the spotlight was a gut punch to the community.

Of course, if you can’t beat them, join them, and so we did. That line of research, “robotics meets LLMs,” could have turned out extremely shallow: maybe you could use a language model to talk to your robot; or have your robot recite Klingon poetry. Big deal. But what actually happened would turn out to be the biggest surprise of my career: the connections ran deep, so deep in fact that to this day we’ve only started to scratch the surface.

It is a common mistake to think of LLMs as being about “language.” Language is indeed the surface form they primarily use (as well as code) but the superpower of an LLM is all about commonsense reasoning: LLMs know simple truths such as “a book belongs on a shelf, not in a bathtub,” or “how one would go about making coffee,” and that turns out to be a big deal for embodied agents trying to act in the real world. So it’s no surprise that the first corner of robotics to be affected by LLMs would be planning.

It may help to draw a diagram of how a robot works conceptually. I am sure that I won’t make many friends in the community by (over-)simplifying things to this degree, but in the spirit of “all models are wrong, but some are useful,” here is one I find particularly illuminating. Picture a loop where your robot perceives the state of the world, sends that state to a planner, which, in combination with a stated goal, writes a plan to achieve it. That plan gets sent to a robot controller, which is in charge of executing it by actuating the hardware. Of course, the world keeps on changing, so maybe only the first steps of that plan get executed, until the state estimate gets updated, the robot replans, executes the next steps, and so on.

This is a very rough sketch that has the merit of mapping on to the major subfields in robotics: state estimation, task and motion planning, and control. Each has traditionally developed in parallel, and many would argue that this resulted in system-level issues being largely ignored and problems being tossed around like a hot potato across fields: too many TAMP papers taking perfect state estimation as a given, too many control strategies happy to summarily reject a plan they can’t execute — and don’t get me started on trying to get gradients to flow across those boundaries!

So of course the first disruption came for the planner. I am probably biased, but I’ll single out SayCan as the “aha” moment where the community realized that if we lifted much of planning into “semantic space,” as opposed to trying to do it in geometric space, we could use LLMs to do the job, and inherit all the benefits of their common sense abilities without having to collect any data, craft robot-specific ontologies or build symbolic reasoning engines.

Once your interfaces to both the perception and actuation use natural language, it’s very tempting to use language as the de-facto API for everything. And language has a lot going for it: it’s flexible, it’s interpretable, it can describe things at any level of abstraction you choose. The last of which was a huge problem for fixed APIs: it may be ok for the world to look like a collection of bounding boxes to a self-driving car for instance, but as soon as you’re actually trying to make contact with objects, you probably want richer geometry and semantics. Maybe the planner doesn’t know in advance what information would be useful for the perception module to provide. Maybe it should be a two-way conversation …

Which brings me to the next stage of that journey: let’s have the planner and the perception system both use natural language. Those VLMs are getting really good, let’s leverage them and make that two-way conversation an actual dialog. This is the idea behind Socratic Models, where a consensus about what the state of the world, and how to act on it, can be achieved through dialog between models. Inner Monologue took the concept further by making periodic state reestimation and replanning part of that conversation.

Once you have an LLM as the backbone of your robot intelligence, you can do lots of new things. For instance, with AutoRT, we used the LLM to dream up new tasks to perform, which immediately raised the question: if the robot comes up with its own things to do, how do we ensure they’re safe and beneficial? We can prompt the LLM with specific concepts of safety (“don’t pick up sharp objects”) or even more general human-centered values: “you may not injure a human being …” Sound familiar? If you had told me a couple of years ago that we would have a not-entirely implausible path to implementing Asimov’s laws of robotics on an actual robot, I would not have believed you. Time will tell if using Constitutional AI as part of a robot’s safety stack is practical, but the fact that we can even talk about it and evaluate it in the real world is unprecedented.

What about the actuation component? Can we chip at that final bastion of traditional robotics and give it the LLM treatment as well? One thing LLMs are really good at is generating code, and at the end of the day, controller software is just that: a piece of code describing a policy. This is where the concept of Code as Policies comes in, the idea that you can prompt an LLM with low-level control APIs and let it describe the actual policy to execute.

Code LMs do that zero-shot very well, provided you’re proficient in the dark arts of prompt design. You can use a dialog strategy to iterate on prompts, as was done in early ChatGPT for Robotics experiments from our colleagues at Microsoft. But it’s even better when you can close the loop and fine-tune your Code LM based on interactive prompting and refinement of your control behaviors. This is something we dubbed Language Model Predictive Control by analogy to classic Model Predictive Control. Not only does this enable models to perform better zero-shot on novel tasks, but it also enables them to learn faster from user interactions.

Once this picture of various LLMs engaged in an internal chat room emerges as the backbone of the robot, it is fair to question if the factorization of the problem into three components with distinct roles is still useful: neural networks can communicate with each other through high-bandwidth, differentiable representations, why force them to collapse them down to words? You do gain some degree of interpretability, but the information loss is significant. Picture for instance that your planner is still essentially blind. Can we merge some of these components? Not out of end-to-end zealotry, but because there is already inherent modularity in these models, thanks to the way different components of a transformer attend to each other, allowing us to reproduce this ‘separation of concerns’ within the neural network itself.

The first experiment in this direction attempted to merge perception and planning with PaLM-E.

It worked remarkably well, in that there were clear observed gains from joint training of the perception and planning modules, as well as evidence of transfer across tasks and embodiments.

The next experiment was to merge perception and actuation, while leaving the planner (which needs to be a large enough model to be useful) out of the loop. Many papers have come up with “pixels to action” models, but for us the transformative approach was RT-1. So much has been happening in recent months in this space, with approaches like Action Diffusion from TRI, Humanoid Transformer from Berkeley, ACT and Octo from Stanford, it has been wonderful to see the explosion in performance and capabilities.

By now you see where this is going: why stick to half measures when you can go all the way and train a single “robot brain” that does everything. Our first attempt at this was RT-2, and it really demonstrated how much being able to reason jointly about the entire problem, while still leveraging non-robotics data sources (internet data for perception and semantic understanding in particular,) benefited the end result. VC-1 from our colleagues at Meta was another notable step in that general direction. I expect many more in the future now that the open-source ecosystem for multimodal models is blossoming, and people are exploring how far we can push these model’s spatial reasoning abilities.

Where do we go from here? The semi-supervised revolution has come and gone. RL is still licking its wounds, with Diffusion Models giving it a good run for its money and Offline RL mounting a comeback. It’s clear that despite marked improvements in data efficiency, which enabled us to envision operating “in the real,” as opposed to having to bet everything on sim-to-real approaches, we’re still data bound, and improving the efficiency and diversity of data collection is key.

There lies the biggest tension in the field today: on one hand, we’re seeing that cross-embodied models work amazingly at transferring capabilities across robots, which argues for dialing up the variety of robots, tasks, and taking a diversity-focused approach to the problem. On the other hand, more and more people are clamoring for the “one embodiment to rule them all” approach to robot learning, with literally billion dollars of investment going into generalist robots such as Tesla, Figure, 1X, Agility, Unitree, Sanctuary, Apptronik and many others. The upside of that latter approach is universal capabilities that are particularly suited to learn from human embodiments and be deployed in human spaces. The downside is that you end up putting building, deploying, and maintaining a very complex and expensive piece of hardware in the critical path of scaling your data collection, and significantly raising the bar for the economics of the end product to make sense.

That’s a risky bet, particularly if the cross-embodiment hypothesis turns out to be true and a swarm of cheap robots, as exemplified by experiments like Aloha, UMI, Stretch (and Dobb.E,) Mobile Aloha and Aloha 2, could completely disrupt the field and bring dexterous capabilities to a wide variety of cheaper embodiments. But I would not put my money 100% on either side of that bet at this point: the months ahead are going to be critical to informing where the field should go: diversity vs universality, cheap and scrappy vs high-DOF and full-featured. The world we’re in today is a bit of both: “universal” arms are widely deployed, but the economics of making them worthwhile are brutal, and they generally require bespoke tooling and systems integration to make them actually useful.

One conviction I am developing in the context of data scaling is that generative models are the future of simulation, and that instead of just “better simulators” we should also be chasing how to make generative 3D and video respect not only appearance, but physics and spatial relationships. Every other class of physics simulator out there is being disrupted by generative models, from weather forecasting to protein folding. If instead of having to spend hours authoring a digital replica of my robot and environment, I could capture my robot’s sensors and simply press “play” to generate possible futures, as we did for instance in Video Language Planning, we could solve both the “sim to real” gap and scene authoring problem in one fell swoop.

I am also becoming increasingly convinced that data scaling is largely turning into an HRI problem. Perhaps not the exact problem the HRI community tends to worry about today, however; most of HRI concerns itself with end-users interacting with robots. We need better HRI approaches to designing new and diverse tasks, robustly collecting data, and refining behaviors: improving and streamlining all the careful design that is required to collect data to train models and behaviors, even before an end user even begins to interact with the final product. And we’ve just given the HRI community a golden opportunity to break new ground, by essentially turning every robot out there into a chatbot with eyes, arms, and legs.

Workshops

• Chelsea Finn and Vincent Vanhoucke are speaking at the 2nd Workshop on Pre-Training for Robot Learning and TaskWorkshop@CoRL23.
• Nicolas Heess, Sergey Levine and Chelsea Finn are speaking at the workshop Towards Reliable and Deployable Learning-Based Robotic Systems,
• LangRob @ CoRL 2023: Fei Xia is a speaker. Ted Xiao is an organizer. RoboVQA is presented as an Oral and poster. PromptBook and KnowNo are presented as a poster.
• RT-Trajectory is presented as a poster at OODWorkshop@CoRL23.
• Pete Florence is speaking at NeuRL-RMW: Workshop for Neural Representation Learning for Robot Manipulation.
• Sergey Levine is speaking and Quan Vuan is presenting a poster at Towards Generalist Robots — CoRL23.
• Tuomas Harnooja and Saminda Abeyruwan are speaking at RoboLetics: Workshop on Robot Learning in Athletics @CoRL 2023.

Satellite Events

MuJoCo Meetup

• Announcement: https://github.com/google-deepmind/mujoco/discussions/1140
• RSVP : https://rsvp.withgoogle.com/events/mujoco-corl-2023
• Monday Nov 6th, Google ATL Office.

RT-X / Open X-Embodiment Meetup

• Open to all: Tuesday 1–1:45 PM, Main Conference Hotel in Muse 2.

Main Conference

Organizers

Jie Tan, David D’Ambrosio, Carolina Parada

Board

Vincent Vanhoucke (President), Raia Hadsell (Treasurer), Sergey Levine (Director)

ALOHA Demo at the Google DeepMind Booth

Keynotes

• “Revising Moravec’s Paradox”, Chelsea Finn
• “Bitter Lessons & Sweet Future in Robot Learning”, Karol Hausmann

Industry talk

“Open X-Embodiment and RT-X”, Quan Vuan and Chelsea Finn

Orals

Language to Rewards for Robotic Skill Synthesis

Wenhao Yu, Nimrod Gileadi, Chuyuan Fu, Sean Kirmani, Kuang-Huei Lee, Montse Gonzalez Arenas, Hao-Tien Lewis Chiang, Tom Erez, Leonard Hasenclever, Jan Humplik, Brian Ichter, Ted Xiao, Peng Xu, Andy Zeng, Tingnan Zhang, Nicolas Heess, Dorsa Sadigh, Jie Tan, Yuval Tassa, Fei Xia

Robots That Ask For Help: Uncertainty Alignment for Large Language Model Planners

Allen Z. Ren, Anushri Dixit, Alexandra Bodrova, Sumeet Singh, Stephen Tu, Noah Brown, Peng Xu, Leila Takayama, Fei Xia, Jake Varley, Zhenjia Xu, Dorsa Sadigh, Andy Zeng, Anirudha Majumdar

Posters

Q-Transformer: Scalable Offline Reinforcement Learning via Autoregressive Q-Functions

Yevgen Chebotar, Quan Vuong, Alex Irpan, Karol Hausman, Fei Xia, Yao Lu, Aviral Kumar, Tianhe Yu, Alexander Herzog, Karl Pertsch, Keerthana Gopalakrishnan, Julian Ibarz, Ofir Nachum, Sumedh Sontakke, Grecia Salazar, Huong T Tran, Jodilyn Peralta, Clayton Tan, Deeksha Manjunath, Jaspiar Singht, Brianna Zitkovich, Tomas Jackson, Kanishka Rao, Chelsea Finn, Sergey Levine

Contrastive Value Learning: Implicit Models for Simple Offline RL

Bogdan Mazoure, Benjamin Eysenbach, Ofir Nachum, Jonathan Tompson

RoboPianist: Dexterous Piano Playing with Deep Reinforcement Learning

Kevin Zakka, Philipp Wu, Laura Smith, Nimrod Gileadi, Taylor Howell, Xue Bin Peng, Sumeet Singh, Yuval Tassa, Pete Florence, Andy Zeng, Pieter Abbeel

Online Learning for Obstacle Avoidance

David Snyder, Meghan Booker, Nathaniel Simon, Wenhan Xia, Daniel Suo, Elad Hazan, Anirudha Majumdar

Navigation with Large Language Models: Semantic Guesswork as a Heuristic for Planning

Dhruv Shah, Michael Equi, Blazej Osinski, Fei Xia, Brian Ichter, Sergey Levine

Scaling Up and Distilling Down: Language-Guided Robot Skill Acquisition

Huy Ha, Pete Florence, Shuran Song

RT-2: Vision-Language-Action Models Transfer Web Knowledge to Robotic Control

Anthony Brohan, Noah Brown, Justice Carbajal, Yevgen Chebotar, Xi Chen, Krzysztof Choromanski, Tianli Ding, Danny Driess, Avinava Dubey, Chelsea Finn, Pete Florence, Chuyuan Fu, Montse Gonzalez Arenas, Keerthana Gopalakrishnan, Kehang Han, Karol Hausman, Alexander Herzog, Jasmine Hsu, Brian Ichter, Alex Irpan, Nikhil Joshi, Ryan Julian, Dmitry Kalashnikov, Yuheng Kuang, Isabel Leal, Lisa Lee, Tsang-Wei Edward Lee, Sergey Levine, Yao Lu, Henryk Michalewski, Igor Mordatch, Karl Pertsch, Kanishka Rao, Krista Reymann, Michael Ryoo, Grecia Salazar, Pannag Sanketi, Pierre Sermanet, Jaspiar Singh, Anikait Singh, Radu Soricut, Huong Tran, Vincent Vanhoucke, Quan Vuong, Ayzaan Wahid, Stefan Welker, Paul Wohlhart, Jialin Wu, Fei Xia, Ted Xiao, Peng Xu, Sichun Xu, Tianhe Yu, Brianna Zitkovich

Open-World Object Manipulation using Pre-Trained Vision-Language Models

Austin Stone, Ted Xiao, Yao Lu, Keerthana Gopalakrishnan, Kuang-Huei Lee, Quan Vuong, Paul Wohlhart, Sean Kirmani, Brianna Zitkovich, Fei Xia, Chelsea Finn, Karol Hausman

Gesture-Informed Robot Assistance via Foundation Models

Li-Heng Lin , Yuchen Cui, Yilun Hao, Fei Xia, Dorsa Sadigh

Semantic Mechanical Search with Large Vision and Language Models

Satvik Sharma, Huang Huang, Kaushik Shivakumar, Lawrence Yunliang Chen, Ryan Hoque, brian ichter, Ken Goldberg

Large Language Models as General Pattern Machines

Suvir Mirchandani, Fei Xia, Pete Florence, Brian Ichter, Danny Driess, Montserrat Gonzalez Arenas, Kanishka Rao, Dorsa Sadigh, Andy Zeng

Language to Rewards for Robotic Skill Synthesis

Wenhao Yu, Nimrod Gileadi, Chuyuan Fu, Sean Kirmani, Kuang-Huei Lee, Montse Gonzalez Arenas, Hao-Tien Lewis Chiang, Tom Erez, Leonard Hasenclever, Jan Humplik, Brian Ichter, Ted Xiao, Peng Xu, Andy Zeng, Tingnan Zhang, Nicolas Heess, Dorsa Sadigh, Jie Tan, Yuval Tassa, Fei Xia

Robots That Ask For Help: Uncertainty Alignment for Large Language Model Planners

Allen Z. Ren, Anushri Dixit, Alexandra Bodrova, Sumeet Singh, Stephen Tu, Noah Brown, Peng Xu, Leila Takayama, Fei Xia, Jake Varley, Zhenjia Xu, Dorsa Sadigh, Andy Zeng, Anirudha Majumdar

Geometry Matching for Multi-Embodiment Grasping

Maria Attarian, Muhammad Adil Asif, Jingzhou Liu, Ruthrash Hari, Animesh Garg, Igor Gilitschenski, Jonathan Tompson

General Part Assembly Planning

Yulong Li, Andy Zeng, Shuran Song

FindThis: Language-Driven Object Disambiguation in Indoor Environments

Arjun Majumdar, Fei Xia, Brian Ichter, Dhruv Batra, Leonidas Guibas

What follows is the description of an experimental training curriculum aimed at improving interpersonal effectiveness, which my team took part in a few years ago with extremely good results. In presenting it here, I hope to inspire more interest in targeting such skills as an effective tool for enhancing both team dynamics and individual psychological safety.

Introduction

Workplace education programs typically focus on either team bonding or leadership development. Comparatively little attention has been given to interpersonal skills: how people communicate their needs, their concerns and aspirations, and how they respond to adversity and conflict.

This can be a particular concern in more technical disciplines, where interpersonal communication skills are often not sufficiently represented as part of technical job proficiency training and evaluations. Anyone who has ever been part of an engineering organization, however, would likely agree that gaps in these skills are often a major factor in the overall team’s effectiveness and technical output. Fostering high levels of psychological safety at work is crucial, and people rightfully expect employers to be an active participant in fostering that culture.

A popular misconception is that these soft skills cannot be taught. There is ample evidence that they can, which largely comes from the vast literature of clinical psychology. While this literature typically targets individuals with severe interpersonal communication deficiencies, brought about by psychopathology or addiction, many of the techniques and strategies that are deployed in these clinical settings are surprisingly well-matched to non-clinical up-skilling of otherwise healthy populations.

I describe here an experimental curriculum, developed by clinical psychologists, which leverages the principles of behaviorism to teach strategies to improve interpersonal skills. Example skills include shaping, reinforcement, validation, assertiveness, as well as managing conflict and acceptance.

In a pilot experiment conducted in a software engineering and research team, we measured marked improvements in various metrics of communication and well-being, suggesting that interpersonal effectiveness skills could be a choice, under-appreciated target for workplace training programs.

Program Description

The curriculum progressively builds a vocabulary and set of tools which start from general strategies for influence and relationship building, to more specific skills for asserting oneself and conflict management, concluding with skills pertaining to the regulation of one’s own reactions through deep acceptance and self-reflection.

Principles of Behaviorism

Any intervention aimed at changing an individual’s posture towards interpersonal relationships begins with understanding the fundamental levers one can employ to affect behaviors, such as:

• Reinforcement: providing a reward for desired behavior that functions to increase the probability that the behavior will be repeated.
• Shaping: the progressive reinforcement of approximations to the desired behavior, aiming to steer towards it.
• Extinction: the removal of reinforcements that are (often unintentionally) maintaining a behavior.
• Punishment: maintaining contingencies for ineffective, dangerous, or problematic behavior.

Many individuals will readily recognize behavioral principles like positive and negative reinforcement; however, few understand the finer points (i.e., timing, specificity, etc.) around how to administer them effectively. Given the skill reinforcement requires and our innate “negativity bias” toward aversive stimuli, most people inadvertently focus on punishing behavior they don’t like in others rather than reinforcing that which they do. While punishment can certainly function to change behavior in the right context, it does so at the expense of the relationship, and will backfire if not balanced with reinforcement.

Similarly, principles like shaping and extinction, which are widely used and appreciated in the context of animal training and parenting, are rarely considered or used effectively to manage problematic interpersonal behaviors in adults.

Training in how to effectively apply principles of behaviorism, such as those listed above, was at the foundation of our program and provided a common “language,” with which to explain and conceptualize the remaining inter and intra personal strategies. It may come as a surprise that a curriculum aimed at improving interpersonal relationships would begin by providing tools aiming at inducing behavior change in others. As a motivating example, consider how using “please” to add humility to one’s request on another makes the other person more willing to consider the request. Even when not intentionally using these strategies, we are inadvertently nudging our colleagues to be more or less likely to collaborate with us effectively. Understanding these “rules of the road” for interpersonal interactions brings these choices into conscious awareness instead of up to chance or bad habits.

One natural concern would be that anyone witnessing another colleague subsequently deploy the techniques presented in the curriculum on them would feel manipulated and react negatively, or that the tactics used would merely lose their effectiveness as a result. On the contrary, we observed that having a shared vocabulary provides structure and shared understanding of how to approach difficult conversations that might otherwise be avoided. When it comes to people’s reactions to intervention or manipulation, people were pretty quick to identify phoniness, and we didn’t see anything during the course of the training that changed that dynamic. Sincerity, on the other hand, was powerful when combined with the transparent use of strategies from the course, presumably because the effort and authenticity reflect an awareness of the other person’s experience and an investment in the relationship. In our experimental cohort, people would frequently explicitly label what technique they were deploying during an exchange, as a device for grounding the conversation. As an illustration, “I really appreciated you reviewing my code so quickly, it helped me get my project done before the deadline. Hoping to reinforce this, I am sending my friend an email to poke them to reply to your email that you mentioned you’ve been waiting on.”

Validation

The next critical component of the program was training in validation. Whereas behaviorism focuses on behavioral change, validation is about acceptance. In a sentence, validation communicates awareness, understanding, and concern for another person and/or their position. It demonstrates acceptance, not agreement or approval. When done effectively, validation can inoculate a disagreement from being construed as neglect or disinterest from the other person’s perspective.

Validation can be applied deliberately and liberally in almost any conversation. It has proven to foster collaboration, decrease conflict, and increase psychological safety in dynamics ranging from detainee interrogations to customer service disputes, yet is not widely acknowledged as a tool or commonly deployed in technical or business conversations.

There are various degrees to which one can communicate validation; from simple non-verbal cues (e.g. nodding), to more proactive strategies such as actively reflecting back a statement to a speaker. In addition to validating behaviors, feelings, or thoughts, participants learned simple strategies to soften collaboration through attitudinal and verbal cues. Exploring this palette and associated levels of intensity lays the foundation for much stronger relationship building.

Goals, Relationships and Self-respect

Interpersonal communication is often trying to balance three objectives:

• Achieving a goal
• Improving the relationship
• Preserving one’s self-respect

These goals are not mutually exclusive, and it may be possible to achieve all three even in very challenging situations. Participants thus learned how to define and prioritize objectives and deploy strategies towards achieving them. The ability to prioritize objectives is considered an important first step in toward effective communication. Imagine an employee asking for a raise from their manager. How important is getting the raise relative to preserving a good relationship with the manager? Is it more about the money or the recognition of their work (self-respect)? One’s objectives and priorities in this situation will determine how best to approach the conversation.

Assertiveness

A common challenge of interpersonal communication is asserting one’s self in a manner that is constructive in terms of one’s objectives while maintaining, or even strengthening, the relationship and self -respect. The FEAT strategy for asserting requests or saying “no” to others, is designed to do just that::

• Focus on Facts: Describing the situation objectively.
• Emote: Communicating one’s own emotion,
• Assert: Make a succinct and direct request,
• Treat: Rewarding or reinforcing the positive outcome.

Going in-depth into each of these steps is beyond the scope of this summary. Generally speaking FEAT provides a template anyone can use to assert themselves and pattern-match across situations that might otherwise be difficult or stressful to navigate.

Conflict Management

Conflict is unavoidable, but equipping someone with effective tools in managing it can have a material impact on their ability to reach a resolution.

The focus of the approach is in managing conflicts and disagreements to a stable outcome, where the spotlight can remain on the causes of the conflict (e.g. divergence of opinions or priorities), rather than the character or personalities of those involved. Normalizing conflict and providing people strategies to navigate them without escalation is an essential part of maintaining a high-level of interpersonal fluency. To this end, the curriculum introduced a taxonomy of the interpersonal dynamics based on the well-established research of marriage experts John and Julie Gottman that commonly lead to and amplify conflict:

• Criticism: Attacking someone’s character,
• Defensiveness: Denying any wrongdoing,
• Stonewalling: Disengaging while the other is still engaged,
• Contempt: Communicating disgust, disdain or superiority.

Participants learned how to identify these communication patterns, and develop various strategies for both prevention and remediation against them.

Another aspect of conflict management that isn’t commonly mastered is the art of apologizing for mistakes or wrong doing. An apology’s effectiveness can be deeply influenced by the manner in which it is delivered, and developing a comprehensive tactical plan to deliver an apology can markedly magnify its positive impact. Given the impact of apologizing and the relative lack of education around how to do it, participants learned evidence-based skills for communicating remorse, and how to effectively repair or improve relationships following conflict.

Change, Deep Acceptance and Self-Checking

While the main aspects of interpersonal relationship management naturally pertain to communication strategies, another crucial aspect is to develop skills for managing the self in the face of circumstances that are not entirely under one’s control. Participants thus learned various strategies to help them understand their reactions and cultivate acceptance.

The first set of strategies pertain to analyzing one’s own behavior when emotions are running high. Providing participants with a framework to analyze both the causes and consequences of their behavior in the context of interpersonal communication was considered a first step in enabling them to tailor their toolkit to their own specific needs and circumstances.

Another useful skill is the ability to accept unavoidable setbacks. How one manages when, for example, a consensus opinion doesn’t go their way, can have a material impact in maintaining future relationships and the individual’s burnout. Participants in our program learned strategies to overcome cognitive and emotional resistance when warranted to help them accept difficult conditions, rather than avoid or deny them.

A final skill which supports interpersonal relationships is the ability to effectively change one’s own behavior when it is counterproductive. Participants learn the very simple-to-remember strategy of acting opposite to impulses that conflict with one’s objective. Acting opposite is easy to implement on instinct and broadly applicable to scenarios where a person’s natural emotional inclinations might otherwise impede their effectiveness.

Summary

This condensed overview of the material presented in our interpersonal effectiveness training program is succinct by necessity, and by no means prescriptive. Fully developing these themes would fill the pages of a book.

My main objective is to dispel the notion that interpersonal effectiveness is a ‘black art’ which can not be taught, practiced or cultivated. Below, I provide some evidence, collected via a pilot implementation of this program, supporting these claims.

Experimental Validation

Beginning in February 2020, employees within a 80 person work group were encouraged to take part in the interpersonal effectiveness skills training program following the curriculum introduced above. The training and the coaching sessions were very well received and were associated with positive memories 18 month after it concluded:

We surveyed participants before, immediately after, and 18 months after the conclusion of the training in order to measure their self-reported sense of competency on the skills covered by the training. Participants rated the questions on a 5-point Likert scale (Strongly Disagree, Disagree, Neutral, Agree, Strongly Agree). I report here the fraction of positive responses (Agree, Strongly Agree) as well as the p-value (in parentheses) on the full 5-point scale obtained using a one-sided permutation test. Bolded figures are significant at the 5% level. We did not attempt to control for people transferring out of the group in the intervening time.

[1] Before and after asked about the past 3 months. 18 month later asked about the past 12 months.

The table above reports self-reported competency of the participants in regards to their interactions with their work group. Considered in aggregate, we find that the training significantly improved this competency (p<0.001), and that this effect was still present after 18 months (p<0.02).

When it comes to interactions with managers, reported in this next table, the effect was initially significant in aggregate (p<0.01). The effect was no longer measurable after 18 months (p>0.8). We suspect significant changes in the reporting structure within the team, which we didn’t attempt to control for, may have markedly affected this latter result.

The diminishing returns over time are worth highlighting as a potential for intervention. Refreshers, practice workshops, or periodic exposure to the material may be beneficial for securing the long-term impact of the training. Participants have noted anecdotally that they wished for new team members who had joined later to undergo the same training program in order to maintain a shared foundation for interpersonal relationships within the team.

One unexpected anecdotal observation was that team members seemingly ended up favoring collaborations with colleagues who had gone through this shared experience over others. This multiplier effect, when both sides of the relationship had gone through the same training, is a key value proposition of the approach, and suggests that training leaders alone is insufficient in addressing the combinatorially large set of pairwise interactions that take place every day in the workplace.

Challenges

The main challenge in implementing such training is how to do it at scale. The value of introducing these interpersonal communication strategies is only fully realized when they are internalized through active practice. As a result, a significant fraction of this curriculum was delivered through weekly practice sessions involving direct coaching by professionals, which are costly and time-consuming.

Conclusion

Interpersonal communication is a key component of high-functioning teams. It is surprising how little that skillset tends to be cultivated in the workplace. Here, I attempted to sketch one positive experiment with building a curriculum dedicated to enhancing the proficiency of a team through improving communication. I hope to spur interest in exploring more avenues for this specific type of intervention. While this was framed as a training to enhance team communication, the principles developed in this training are not limited to workplace interactions and are generally applicable and useful to daily life. They have definitely positively impacted my own.

Acknowledgments

This curriculum was designed by Dr Caroline Fleck and Dr Soo Uhm, with significant contributions from Chris Harris. Margaret Lawton and Shivi Singh contributed to the program’s implementation and survey gathering. This article includes significant contributions from Caroline Fleck, Chris Harris and Soo Uhm. Errors or misrepresentations are all mine.