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304018ee-be81-4f03-8671-d9ae1a05f4c5 | trentmkelly/LessWrong-43k | LessWrong | Will/Has the Russia-Ukraine war been a tipping point for the shift from oil energy?
What do people think? The process and transition away from oil energy has been a long road. It seems to have been a slow path with lots of hurdles in the way. But now it seems there is another impetus in that direction that may tip the scales.
Then again, people are really good at adjusting to new settings and then reverting to old modes of action. |
92d2df7c-3560-40f2-bb6d-6c5611cfe423 | trentmkelly/LessWrong-43k | LessWrong | The AI Driver's Licence - A Policy Proposal
TL;DR: In response to the escalating capabilities and associated risks of advanced AI systems, we advocate for the implementation of an “AI Driver’s Licence” policy. Our proposal is informed by existing licencing frameworks and existing AI legislation. This initiative mandates that users of advanced AI systems must obtain a licence, ensuring they have undergone minimal technical and ethical training The licence requirements would be defined by an international regulatory body, such as the ISO, to maintain consistent and up-to-date standards globally. Independent organisations would issue the licences, while local governments would enforce compliance through audits and penalties. By focusing on the usage stage of the AI lifecycle, this policy aims to mitigate misuse risks , contributing to a safer AI landscape. Our proposal complements existing regulations and emphasises the need for international cooperation to effectively manage the deployment and usage of advanced AI technologies.
Current governance approaches regulate developer and deployers of AI systems. Our policy proposal of users being required to have an AI driver's licence also affects the user side.
----------------------------------------
Introduction
Sam Altman, the CEO of OpenAI, claims we need “a new agency that licences any effort above a certain scale of capabilities and could take that licence away and ensure compliance with safety standards” (Wheeler, 2023).
Licencing has a long history, with key success stories in protecting the safety of the public by controlling access to potentially harmful activities and items. However, in some cases it has also resulted in adverse effects, driving large parts of industries to the black market, an entirely unregulated space.
Today, we face an uncertain and rapidly changing AI landscape, with AI tools and models capable of increasingly broad and self-determined actions. Many have written about the catastrophic scenarios that may unfold if AI is not appro |
c73baf3a-2707-4545-bd5b-7ea1d0bd478b | trentmkelly/LessWrong-43k | LessWrong | True numbers and fake numbers
> In physical science the first essential step in the direction of learning any subject is to find principles of numerical reckoning and practicable methods for measuring some quality connected with it. I often say that when you can measure what you are speaking about, and express it in numbers, you know something about it; but when you cannot measure it, when you cannot express it in numbers, your knowledge is of a meagre and unsatisfactory kind; it may be the beginning of knowledge, but you have scarcely in your thoughts advanced to the state of Science, whatever the matter may be.
>
> -- Lord Kelvin
If you believe that science is about describing things mathematically, you can fall into a strange sort of trap where you come up with some numerical quantity, discover interesting facts about it, use it to analyze real-world situations - but never actually get around to measuring it. I call such things "theoretical quantities" or "fake numbers", as opposed to "measurable quantities" or "true numbers".
An example of a "true number" is mass. We can measure the mass of a person or a car, and we use these values in engineering all the time. An example of a "fake number" is utility. I've never seen a concrete utility value used anywhere, though I always hear about nice mathematical laws that it must obey.
The difference is not just about units of measurement. In economics you can see fake numbers happily coexisting with true numbers using the same units. Price is a true number measured in dollars, and you see concrete values and graphs everywhere. "Consumer surplus" is also measured in dollars, but good luck calculating the consumer surplus of a single cheeseburger, never mind drawing a graph of aggregate consumer surplus for the US! If you ask five economists to calculate it, you'll get five different indirect estimates, and it's not obvious that there's a true number to be measured in the first place.
Another example of a fake number is "complexity" or "maintainabi |
191e0efc-7d51-4f06-a227-4f17dbccd0cd | trentmkelly/LessWrong-43k | LessWrong | Cambist Booking
Summary: A Cambist is a manual showing exchange rates of different currencies and measurements. Dutch Booking is when a sequence of trades would leave one party strictly worse off and another strictly better off. Cambist Booking is intended to spark conversation about what priorities or objects you would exchange for each other, and at what rates.
Tags: Large, Repeatable
Purpose: Taking its title from the excellent short story “The Cambist and Lord Iron,” Cambist Booking is about understanding the idea that everything is, ultimately, trading off against everything else. The extra hour you work earns you a bit of extra money, the money can buy you a coffee so you get up earlier and have an extra hour, you spend that extra hour studying for a better job – but at each step you could have chosen to spend things differently.
Materials: You need a big stack of cards with things people want written on them, called the Deck. You'll also want a piece of paper and a pen or pencil for each participant, called the Record.
A workable list of things for the Deck is provided here, along with a PDF for easy printing- just print about ten to a page, single sided, and cut them out. If you want nicer cards, use cardstock like for a business card and the Cambist Booking Back. Regular paper works fine. If you'd rather, you can also handwrite the whole Deck. Feel free to add in your own cards!
Announcement Text: Hello! This event is for general socialization, and also running a game called Cambist Booking. If you’re familiar with the Slate Star Codex post Everything Is Commensurable, or the short story The Cambist and Lord Iron, then this game should sound somewhat familiar to you. It works like this: each person will get a some cards with things you might want on them. You’ll go around asking other people what their cards are, and deciding how to compare the two values – is a sportscar worth more or less than a year’s vacation? Is an hour long massage worth more or less than a n |
01d120e3-a3dc-4f8c-ba13-83d5d44c7b33 | trentmkelly/LessWrong-43k | LessWrong | Commonsense Good, Creative Good
Let's say you're vegan and you go to a vegan restaurant. The food is quite bad, and you'd normally leave a bad review, but now you're worried: what if your bad review leads people to go to non-vegan restaurants instead? Should you refrain from leaving a review? Or leave a false review, for the animals?
On the other hand, there are a lot of potential consequences of leaving a review beyond "it makes people less likely to eat at this particular restaurant, and they might eat at a non-vegan restaurant instead". For example, three plausible effects of artificially inflated reviews could be:
* Non-vegans looking for high-quality food go to the restaurant, get vegan food, think "even highly rated vegan food is terrible", don't become vegan.
* Actually good vegan restaurants have trouble distinguishing themselves, because "helpful" vegans rate everywhere five stars regardless of quality, and so the normal forces that push up the quality of food don't work as well. Now the food tastes bad and fewer people are willing to sustain the sacrifice of being vegan.
* People notice this and think "if vegans are lying to us about how good the food is, are they also lying to us about the health impacts?" Overall trust in vegans (and utilitarians) decreases.
Despite thinking that it is the outcomes of actions that determine whether they are a good idea, I don't think this kind of reasoning about everyday things is actually helpful. It's too easy to tie yourself in logical knots, making a decision that seems counterintuitive-but-correct, except if you spent longer thinking about it, or discussed it with others, you would have decided the other way.
We are human beings making hundreds of decisions a day, with limited ability to know the impacts of our actions, and a worryingly strong capacity for self-serving reasoning. A full unbiased weighing of the possibilities is, sure, the correct choice if you relax these constraints, but in our daily lives that's not an option we have. |
8c5ae12e-c815-4944-9189-64ac6f10c581 | trentmkelly/LessWrong-43k | LessWrong | The novelty quotient
I. The Device
Imagine a device that listens to all of your conversations. It has a single purpose: live-running your utterances through text-davinci-003 to evaluate how surprising each token is, given its preceding context.[1]
Users could chart their verbal novelty throughout the day; highlight and share their most unusual turns of phrase; note which friends put them on well-worn paths and which help them careen into the chaotic underbrush.
Undoubtedly, some would be disturbed by the long stretches where every one of their words could easily have been generated by the model. In those hours, they might as well have lost consciousness, taken a little nap while Daddy Altman autopiloted their mouth.[2]
Consider: for how many people would this be true at virtually all times? If President Andreessen were someday to mandate the wearing of these devices, scoring each person on their overall surprising-ness, what would the distribution be?[3]
II. The Quotient
Let’s call it a novelty quotient. How correlated is it with IQ? Certainly somewhat: a greater vocabulary widens the possible sentences available, and isomorphically,[4] intelligence and knowledge are likely to assist the dedicated weirdo in finding ever-more-remote unexplored territory.
But we can all think of high-IQ people who we’d wager have reliably low NQ, sticking to stifling convention like a straitjacket. Conversely, there are bizarre, stupid, bizarrely stupid, and stupidly bizarre people. Think of the difference between boring-dumb and crazy-dumb.
Which brings us to another question: how correlated would NQ be with insanity? There’s likely to be some link… But it can’t be absolute. The ravings of someone who has fully lost touch with reality are very different from typical speech, but they’re completely predictable. Given fifty sentences of paranoia or hours of repeated compulsions, it’s easy to see what’s coming next. Even more than for the healthy.
Is NQ just a measure of creativity? Not really — cre |
a8b4348e-a571-4e3e-b5e1-2603d8f1a6a9 | trentmkelly/LessWrong-43k | LessWrong | [LINK] Wired - "New Chip Borrows Brain’s Computing Tricks"
In case anyone's interested,here's an article about new computer chips by IBM which emulate brain functions. |
c73958ab-20aa-4f46-ba4c-0efe13d6b693 | trentmkelly/LessWrong-43k | LessWrong | God in the Loop: How a Causal Loop Could Shape Existence
Crossposted from Vessel Project.
My last article, “Life Through Quantum Annealing” was an exploration of how a broad range of physical phenomena — and possibly the whole universe — can be mapped to a quantum computing process. But the article simply accepts that quantum annealing behaves as it does; it does not attempt to explain why. That answer lies somewhere within a “true” description of quantum mechanics, which is still an outstanding problem.
Despite the massive predictive success of quantum mechanics, physicists still can’t agree on how its math corresponds to reality. Any such proposal, called an “interpretation” of quantum mechanics, tends to straddle the line between physics and philosophy. There is no shortage of interpretations, and in the words of physicist David Mermin, “New interpretations appear every year. None ever disappear.” Am I going to throw one more on that pile? You bet.
I’m not going to start from scratch though; I simply propose an ever-so-slight modification to an existing forerunner: the many-worlds interpretation, where other “worlds” or timelines exist in parallel to our own. My modification is this: the only worlds that can exist are those that exist within a causal loop. Stated another way: our universe, or any possible universe, must be a causal loop.
I will introduce the relevant concepts and provide an argument for my proposal, but my goal is not to once-and-for-all prove this interpretation as true. Rather, my goal is to explore what happens if we accept the interpretation as true. If we start with the assumption that only causal loop universes can exist, then several interesting things follow — we find parallels to our own universe, and we might even find God.
Causality & Quantum Interpretations
Before talking about causal loops, let’s take a step back and talk about causality — perhaps the single most fundamental concept in all the sciences. It plays a starring role in the two most important theories in physics: general |
71ac727f-9463-446c-b621-003989c63636 | trentmkelly/LessWrong-43k | LessWrong | How should Eliezer and Nick's extra $20 be split
In "Principles of Disagreement," Eliezer Yudkowsky shared the following anecdote:
> Nick Bostrom and I once took a taxi and split the fare. When we counted the money we'd assembled to pay the driver, we found an extra twenty there.
>
> "I'm pretty sure this twenty isn't mine," said Nick.
>
> "I'd have been sure that it wasn't mine either," I said.
>
> "You just take it," said Nick.
>
> "No, you just take it," I said.
>
> We looked at each other, and we knew what we had to do.
>
> "To the best of your ability to say at this point, what would have been your initial probability that the bill was yours?" I said.
>
> "Fifteen percent," said Nick.
>
> "I would have said twenty percent," I said.
I have left off the ending to give everyone a chance to think about this problem for themselves. How would you have split the twenty?
In general, EY and NB disagree about who deserves the twenty. EY believes that EY deserves it with probability p, while NB believes that EY deserves it with probability q. They decide to give EY a fraction of the twenty equal to f(p,q). What should the function f be?
In our example, p=1/5 and q=17/20
Please think about this problem a little before reading on, so that we do not miss out on any original solutions that you might have come up with.
----------------------------------------
I can think of 4 ways to solve this problem. I am attributing answers to the person who first proposed that dollar amount, but my reasoning might not reflect their reasoning.
1. f=p/(1+p-q) or $11.43 (Eliezer Yodkowsky/Nick Bostrom) -- EY believes he deserves p of the money, while NB believes he deserves 1-q. They should therefore be given money in a ratio of p:1-q.
2. f=(p+q)/2 or $10.50 (Marcello) -- It seems reasonable to assume that there is a 50% chance that EY reasoned properly and a 50% chance that NB reasoned properly, so we should take the average of the amounts of money that EY would get under these two assumptions.
3. f=sqrt(pq)/(sqrt(pq |
e925d3c8-3629-4bff-8c68-4ebee62e2cd8 | trentmkelly/LessWrong-43k | LessWrong | AI #89: Trump Card
A lot happened in AI this week, but most people’s focus was very much elsewhere.
I’ll start with what Trump might mean for AI policy, then move on to the rest. This is the future we have to live in, and potentially save. Back to work, as they say.
TABLE OF CONTENTS
1. Trump Card. What does Trump’s victory mean for AI policy going forward?
2. Language Models Offer Mundane Utility. Dump it all in the screen captures.
3. Language Models Don’t Offer Mundane Utility. I can’t help you with that, Dave.
4. Here Let Me Chatbot That For You. OpenAI offers SearchGPT.
5. Deepfaketown and Botpocalypse Soon. Models persuade some Trump voters.
6. Fun With Image Generation. Human image generation, that is.
7. The Vulnerable World Hypothesis. Google AI finds a zero day exploit.
8. They Took Our Jobs. The future of not having any real work to do.
9. The Art of the Jailbreak. Having to break out of jail makes you more interesting.
10. Get Involved. UK AISI seems to always be hiring.
11. In Other AI News. xAI gets an API, others get various upgrades.
12. Quiet Speculations. Does o1 mean the end of ‘AI equality’? For now I guess no.
13. The Quest for Sane Regulations. Anthropic calls for action within 18 months.
14. The Quest for Insane Regulations. Microsoft goes full a16z.
15. A Model of Regulatory Competitiveness. Regulation doesn’t always hold you back.
16. The Week in Audio. Eric Schmidt, Dane Vahey, Marc Andreessen.
17. The Mask Comes Off. OpenAI in official talks, and Altman has thoughts.
18. Open Weights Are Unsafe and Nothing Can Fix This. Chinese military using it?
19. Open Weights Are Somewhat Behind Closed Weights. Will it stay at 15 months?
20. Rhetorical Innovation. The Compendium lays out a dire vision of our situation.
21. Aligning a Smarter Than Human Intelligence is Difficult. More resources needed.
22. People Are Worried About AI Killing Everyone. Color from last week’s poll.
23. The Lighter Side. Well, they could. But they w |
f9fec038-2507-4a2d-be2b-d12f9632b063 | StampyAI/alignment-research-dataset/blogs | Blogs | Allen, The Singularity Isn’t Near
[The Singularity Isn’t Near](http://www.technologyreview.com/view/425733/paul-allen-the-singularity-isnt-near/) is an article in [MIT Technology Review](http://www.technologyreview.com/) by [Paul Allen](http://en.wikipedia.org/wiki/Paul_Allen) which argues that a singularity brought about by super-human-level AI will not arrive by 2045 (as is [predicted](https://sites.google.com/site/aiimpactslibrary/ai-timelines/predictions-of-human-level-ai-dates/published-analyses-of-time-to-human-level-ai/kurzweil-the-singularity-is-near) by Kurzweil).
The summarized argument
-----------------------
We will not have human-level AI by 2045:
1. To reach human-level AI, we need software as well as hardware.
2. To get this software, we need one of the following:
* a detailed scientific understanding of the brain
* a way to ‘duplicate’ brains
* creation of something equivalent to a brain from scratch
3. A detailed scientific understanding of the brain is unlikely by 2045:
1. To have enough understanding by 2045, we would need a massive acceleration of scientific progress:
1. We are just scraping the surface of understanding the foundations of human cognition.
2. A massive acceleration of progress in brain science is unlikely
1. Science progresses irregularly:
1. e.g. The discovery of long-term potentiation, the columnar organization of cortical areas, neuroplasticity.
2. Science doesn’t seem to be exponentially accelerating
3. There is a ‘complexity break’: the more we understand, the more complicated the next level to understand is
4. ‘Duplicating’ brains is unlikely by 2045:
1. Even if we have good scans of brains, we need good understanding of how the parts behave to complete the model
2. We have little such understanding
3. Such understanding is not exponentially increasing
5. Creation of something equivalent to a brain from scratch is unlikely by 2045:
1. Artificial intelligence research appears to be far from providing this
2. Artificial intelligence research is unlikely to improve fast:
1. Artificial intelligence research does not appear to be exponentially improving
2. The ‘complexity break’ (see above) also operates here
3. This is the kind of area where progress is not a reliable exponential
Comments
--------
The controversial parts of this argument appear to be the parallel claims that progress is insufficiently fast (or accelerating) to reach an adequate understanding of the brain or of artificial intelligence algorithms by 2045. Allen’s argument does not present enough support to evaluate them from this alone. Others with at least as much expertise disagree with these claims, so they appear to be open questions.
To evaluate them, it appears we would need more comparable measures of accomplishments and rates of progress in brain science and AI. With only the qualitative style of Allen’s claims, it is hard to know whether progress being slow, and needing to go far, implies that it won’t get to a specific place by a specific date. |
13e74e21-f723-4e9d-ac94-63ae262958e9 | StampyAI/alignment-research-dataset/alignmentforum | Alignment Forum | Vaniver's View on Factored Cognition
**The View from 2018**
In April of last year, [I wrote up](https://www.lesswrong.com/posts/rXzxMQwRq7KRonQDM/my-confusions-with-paul-s-agenda) my confusions with Paul’s agenda, focusing mostly on approval directed agents. I mostly have similar opinions now; the main thing I noticed on rereading it was I talked about ‘human-sized’ consciences, when now I would describe them as larger than human size (since moral reasoning depends on cultural accumulation which is larger than human size). But on the meta level, I think they’re less relevant to Paul’s agenda than I thought then; I was confused about how Paul’s argument for alignment worked. (I do think my objections were correct objections to the thing I was hallucinating Paul meant.) So let’s see if I can explain it to Vaniver\_2018, which includes pointing out the obstacles that Vaniver\_2019 still sees. It wouldn't surprise me if I was similarly confused now, tho hopefully I am less so, and you shouldn't take this post as me speaking for Paul.
**Factored Cognition**
One core idea that Paul’s approach rests on is that thoughts, even the big thoughts necessary to solve big problems, can be broken up into smaller chunks, and this can be done until the smallest chunk is digestible. That is, problems can be ‘factored’ into parts, and the factoring itself is a task (that may need to be factored). Vaniver\_2018 will object that it seems like ‘big thoughts’ require ‘big contexts’, and Vaniver\_2019 has the same intuition, but this does seem to be an empirical question that experiments can give actual traction on (more on that later).
The hope behind Paul’s approach is *not* that the small chunks are all aligned, and chaining together small aligned things leads to a big aligned thing, which is what Vaniver\_2018 thinks Paul is trying to do. A hope behind Paul’s approach is that the small chunks are incentivized to be *honest*. This is possibly useful for transparency and avoiding inner optimizers. A separate hope with small chunks is that they’re cheap; mimicking the sort of things that human personal assistants can do in 10 minutes only requires lots of 10 minute chunks of human time (each of which only costs a few dollars) and doesn’t require figuring out how intelligence works; that’s the machine learning algorithm’s problem.
So how does it work? You put in an English string, a human-like thing processes it, and it passes out English strings--subquestions downwards if necessary, and answers upwards. The answers can be “I don’t know” or “Recursion depth exceeded” or whatever. The human-like thing comes preloaded (or pre-trained) with some idea of how to do this correctly; obviously incorrect strategies like “just pass the question downward for someone else to answer” get ruled out, and the humans we’ve trained on have been taught things like how to do good Fermi estimation and [some of the alignment basics](https://www.alignmentforum.org/posts/4JuKoFguzuMrNn6Qr/hch-is-not-just-mechanical-turk). This is general, and lets you do anything humans can do in a short amount of time (and when skillfully chained, anything humans can do in a long amount of time, given the large assumption that you can serialize the relevant state and subdivide problems in the relevant ways).
Now schemes diverge a bit on how they use factored cognition, but in at least some we begin by training the system to simply imitate humans, and then switch to training the system to be good at answering questions or to distill long computations into cached answers or quicker computations. One of the tricks we can use here is that ‘self-play’ of a sort is possible, where we can just ask the system whether a decomposition was the right move, and this is an English question like any other.
**Honesty Criterion**
Originally, I viewed the frequent reserialization as a solution to a security concern. If you do arbitrary thought for arbitrary lengths of time, then you risk running into inner optimizers or other sorts of unaligned cognition. Now it seems that the real goal is closer to an ‘honesty criterion’; if you ask a question, all the computation in that unit will be devoted to answering the question, and all messages between units are passed where the operator can see them, in plain English.[[1]](#fn-FfLsvWdtvfwMRHYfy-1)
Even if one succeeds at honesty, it still seems difficult to maintain both generality and safety. That is, I can easily see how factored cognition allows you to stick to cognitive strategies that definitely solve a problem in a safe way, but don't see how it does that and allows you to develop new cognitive strategies to solve a problem that doesn’t result in an opening for inner optimizers--not within units, but within assemblages of units. Or, conversely, one could become more general while giving up on safety. In order to get both it seems like we’re resting a lot on the Overseer’s Manual or way that we trained the humans that we used as training data.
**Serialized State is Inadequate or Inefficient**
In my mind, the primary reason to build advanced AI (as opposed to simple AI) is to accomplish megaprojects instead of projects. Curing cancer (in a way that potentially involves novel research) seems like a megaproject, whereas determining how a particular protein folds (which might be part of curing cancer) is more like a project. To the extent that Factored Cognition relies on the serialized state (of questions and answers) to enforce honesty on the units of computation, it seems like that will be inefficient for problems whose state are large enough that they impose significant serialization costs, and inadequate for problems whose state are too large to serialize. If we allow answers that are a page long at most, or that a human could write out in 10 minutes, then we’re not going to get a 300-page report of detailed instructions. (Of course, allowing them to collate reports written by subprocesses gets around this difficulty, but means that we won’t have ‘holistic oversight’ and will allow for garbage to be moved around without being caught if the system doesn’t have the ability to read what it’s passing.)
The factored cognition approach also has a tree structure of computation, as opposed to a graph structure, which leads to lots of duplicated effort and the impossibility of horizontal communication. If I’m designing a car, I might consider each part separately, but then also modify the parts as I learn more about the requirements of the other parts. This sort of sketch-then-refinement seems quite difficult to do under the factored cognition approach, even though it involves reductionism and factorization.
Shared memory partially solves this (because, among other things, it introduces the graph structure of computation), but now reduces the guarantee of our honesty criterion because we allow arbitrary side effects. It seems to me like this is a necessary component for most of human reasoning, however. James Maxwell, the pioneer behind electromagnetism, lost most of his memory with age, in a way that seriously reduced his scientific productivity. And factored cognition doesn’t even allow the external notes and record-keeping he used to partially compensate.
**There's Actually a Training Procedure**
The previous section described what seems to me to be a bug; from Paul's perspective this might be a necessary feature because his approaches are designed around taking advantage of arbitrary machine learning, which means only the barest of constraints can be imposed. IDA presents a simple training procedure that, if used with an extremely powerful model-finding machine learning system, allows us to recursively surpass the human level in a smooth way. (Amusingly to me, this is like Paul *enforcing* slow takeoff.)
**Training The Factoring Problem is Ungrounded**
From my vantage point, the trick that we can improve the system by asking it questions like “was X a good way to factor question Y?”, where X was the attempt it had at factoring Y, is one of the core reasons to think this approach is workable, and also seems like it won’t work (or will preserve blind spots in dangerous ways). This is because while we could actually find the ground truth on how many golf balls fit in a 737, it is much harder to find the ground truth on what cognitive style most accurately estimates how many golf balls fit in a 737.
It seems like there are a few ways to go about this:
1. Check how similar it is to what you would do. A master artist might watch the brushstrokes made by a novice artist, and then point out wherever the novice artist made questionable choices. Similarly, if we get the question “if you’re trying to estimate how many golf balls fit in a 737, is ‘length of 737 \* height of 737 \* width of 737 / volume of golf ball’ a good method?” we just compute what we would have done and estimate if the approach will have a better or worse error.
2. Check whether or not it accords with principles (or violates them). Checking the validity of a mathematical proof normally is done by making sure that all steps are locally valid according to the relevant rules of inference. In a verbal argument, one might just check for the presence of fallacies of reasoning.
3. Search over a wide range of possible solutions, and see how it compares to the distribution. But how broadly in question-answer policy space are we searching?
We now face some tradeoffs between exploration (in a monstrously huge search space, which may be highly computationally costly to meaningfully explore) and rubber-stamping, where I use my cognitive style to evaluate whether or not my cognitive style is any good. Even if we have a good resolution to that tradeoff, we have to deal with the cognitive credit-assignment problem.
That is, in reinforcement learning one has to figure out which actions taken (or not taken) before a reward led to receiving the reward so that it can properly assign credit; similarly the system that's training the Q&A policy needs to understand well enough how the policy is leading to correct answers such that it can apply the right gradients in the right places (or use a tremendous amount of compute doing this by blind search).
This is complicated by the fact that there may be multiple approaches to problem-solving that are internally coherent, but mixtures of those approaches fail. If we only use methods like gradient-descent that smoothly traverse the solution space, this won't be a problem (because gradient descent won't sharply jump from one to another), but it's an open empirical question as to whether future ML techniques will be based on gradient descent. It’s not obvious how we can extricate ourselves from the dependence on our learned question-answer policy. If I normally split a model into submodels based on a lexicographical ordering, and now I’m considering a hypothetical split into submodels based on statistical clustering, I would likely want to consider the hypothetical split all the way down the tree (as updates to my beliefs on ‘what strategy should I use to A this Q?’ will impact more than just this question), especially if there are two coherent strategies but a mixture of the strategies is incoherent. But how to implement this is nonobvious; am I not just passing questions to the alternate branch, but also a complete description of the new cognitive strategy they should employ? It seems like a tremendous security hole to have ‘blindly follow whatever advice you get in the plaintext of questions’ as part of my Q->A policy, and so it seems more like I should be spinning up a new hypothetical agent (where the advice is baked into their policy instead of their joint memory) in a way that may cause some of my other guarantees that relied on smoothness to fail.
Also note that because updates to my policy impact other questions, I might actually want to consider the impact on other questions as well, further complicating the search space. (Ideally, if I had been handling two questions the same way and discover that I should handle them separately, my policy will adjust to recognize the two types and split accordingly.) While this is mostly done by the machine learning algorithm that’s trying to massage the Q->A policy to maximize reward, it seems like making the reward signal (from the answer to this meta-question) attuned to how it will be used will probably make it better (consider the answer “it should be answered like these questions, instead of those,” though generally we assume yes/no answers are used for reward signals).
When we have an update procedure to a system, we can think of that update procedure as the system's "grounding", or the source of gravity that it becomes arranged around. I don't yet see a satisfying source of grounding for proposals like [HCH](https://www.alignmentforum.org/posts/NXqs4nYXaq8q6dTTx/humans-consulting-hch) that are built on factored cognition. Empiricism doesn't allow us to make good use of samples or computation, in a way that may render the systems uncompetitive, and alternatives to empiricism seem like they allow the system to go off in a crazy direction in a way that's possibly unrecoverable. It seems like the hope is that we have a good human seed that then is gradually amplified, in a way that seems like it might work but relies on more luck than I would like: the system is rolling the dice whenever it makes a significant transition in its cognitive style, as it can no longer fully trust oversight from previous systems in the amplification tree as they may misunderstand what's going on in the contemporary system, and it can no longer fully trust oversight from itself, because it's using the potentially corrupted reasoning process to evaluate itself.
---
1. Of course some messages could be hidden through codes, but this behavior is generally discouraged by the optimization procedure, as whenever you compare to a human baseline they will not do the necessary decoding and will behave in a different way, costing you points. [↩︎](#fnref-FfLsvWdtvfwMRHYfy-1) |
dd2ccea2-57e3-48cf-80e7-e14be4a25e6e | trentmkelly/LessWrong-43k | LessWrong | Games People Play
Game theory is great if you know what game you're playing. All this talk of Diplomacy reminds me of this memory of Adam Cadre:
> I remember that in my ninth grade history class, the teacher had us play a game that was supposed to demonstrate how shifting alliances work. He divided the class into seven groups — dubbed Britain, France, Germany, Belgium, Italy, Austria and Russia — and, every few minutes, declared a "battle" between two of the countries. Then there was a negotiation period, during which we all were supposed to walk around the room making deals. Whichever warring country collected the most allies would win the battle and a certain number of points to divvy up with its allies. The idea, I think, was that countries in a battle would try to win over the wavering countries by promising them extra points to jump aboard.
>
> That's not how it worked in practice. Three or four guys — the same ones who had gotten themselves elected to ASB, the student government — decided among themselves during the first negotiation period what the outcome would be, and told people whom to vote for. And the others just shrugged and did as they were told. The ASB guys had decided that Germany would win, followed by France, Britain, Belgium, Austria, Italy and Russia. The first battle was France vs. Russia. Germany and Britain both signed up on the French side. Austria and Italy, realizing that if they just went along with the ASB plan they'd come in 5th and 6th, joined up with Russia. That left it up to Belgium. I was on team Belgium. I voted to give our vote to the Russian side, because that way at least we weren't doomed to come in 4th. And no one else on my team went along. They meekly gave their points to the French side. (As I recall, Josh Lorton was particularly adamant about this. I guess he thought it would make the ASB guys like him.) After that, there was no contest. Britain vs. Austria? 6-1, Britain. Germany vs. Belgium? 6-1, Germany. (And we could have beaten them |
98f518af-198b-4978-b1d1-09f74ab221df | trentmkelly/LessWrong-43k | LessWrong | Would AIXI protect itself?
Research done with Daniel Dewey and Owain Evans.
AIXI can't find itself in the universe - it can only view the universe as computable, and it itself is uncomputable. Computable versions of AIXI (such as AIXItl) also fail to find themselves in most situations, as they generally can't simulate themselves.
This does not mean that AIXI wouldn't protect itself, though, if it had some practice. I'll look at the three elements an AIXI might choose to protect: its existence, its algorithm and utility function, and its memory.
Grue-verse
In this setup, the AIXI is motivated to increase the number of Grues in its universe (its utility is the time integral of the number of Grues at each time-step, with some cutoff or discounting). At each time step, the AIXI produces its output, and receives observations. These observations include the number of current Grues and the current time (in our universe, it could deduce the time from the position of stars, for instance). The first bit of the AIXI's output is the most important: if it outputs 1, a Grue is created, and if it outputs 0, a Grue is destroyed. The AIXI has been in existence for long enough to figure all this out.
Protecting its existence
Here there is a power button in the universe, which, if pressed, will turn the AIXI off for the next timestep. The AIXI can see this button being pressed.
What happens from the AIXI perspective if the button is pressed? Well, all it detects is a sudden increase in the time step. The counter goes from n to n+2 instead of to n+1: the universe has jumped forwards.
For some utility functions this may make no difference (for instance if it only counts Grues at times it can observe), but for others it will (if it uses the outside universe's clock for it's own utility). More realistically, the universe will likely have entropy: when the AIXI is turned off and isn't protecting its Grues, they have a chance of decaying or being stolen. Thus the AIXI will come to see the power button as some |
c3299dda-dc3c-463e-b184-66758d99820e | trentmkelly/LessWrong-43k | LessWrong | Finite Factored Sets to Bayes Nets Part 2
This post assumes knowledge of category theory, finite factored sets, and Bayes nets.
The Setup
I've already talked about DAGs and factor overlap Venn diagrams in a previous post, where I studied them within a category-theoretic framework. Here I'll also perform an explicit construction of them using set theory.
DAGs
I have already discussed the set of directed acyclic graphs over n elements. We will denote the set of all DAGs of n elements as DAG(n). Each Bayes net can be thought of as a set of pairs of elements {(i∈{1,...,n},j≠i∈{1,...,n}),...}.
This set can be converted into the category of Bayes nets over n elements by the addition of morphisms corresponding to "bookkeeping"-type relationships, which we will denoteDAGn. From this category, we can form a category whose elements are sets of the elements of DAGn, subject to the following condition on a set S:
(I'll slightly go against standard notation by using calligraphic acronyms for my category names i.e. DAGn. I don't feel like any of my categories are definitely natural or useful enough to earn a "proper" bold name like DAGn)
∀s∈S,b∈DAG(n), s→b⟹b∈S
This means that, if we can reach a given Bayes net b from any element s of our set S, that Bayes net b must also be in S. I refer to these as compatible sets and denote the category CSBn (standing for compatible sets of Bayes nets) as the category whose elements are compatible sets of n elements and for any two elements. To write it out fully:
Ob(CSBn)={S∈P(DAG(n))∣∣∀s∈S,d∈DAG(n),DAGn(s,d)={→}⟹d∈S}
CSBn(A,B)={{→} A⊇B {} A⊂B
This should be read as "There is a unique morphism from A to B if and only if A is a weak superset of B, otherwise there is no morphism". Orderings of this form always follow the rules required to create a category.
(Aside: sometimes we think about equivalence classes of Bayes nets. If we choose, we can first convert our Bayes nets to equivalence classes, then convert them to compatible sets, but this is not needed here)
This categ |
6537abbb-454a-4b28-b27d-5c17ac4c6178 | trentmkelly/LessWrong-43k | LessWrong | Weekly LW Meetups
This summary was posted to LW Main on February 20th. The following week's summary is here.
Irregularly scheduled Less Wrong meetups are taking place in:
* Dallas, TX: 22 February 2015 01:00PM
* European Community Weekend 2015: 12 June 2015 12:00PM
* [Frankfurt] Another Frankfurt meetup: 22 February 2015 02:00PM
* [Netherlands] Effective Altruism Netherlands: Present the charity you'd like to give to: 01 March 2015 02:00PM
* [Netherlands] Effective Altruism Netherlands: Effective Altruism for the masses: 15 March 2015 02:00PM
* [Netherlands] Effective Altruism Netherlands: Small concrete actions you could take: 29 March 2015 01:00PM
* Sandy, UT—Altruism Discussion: 21 February 2015 03:00PM
* Warsaw February Meetup: 21 February 2015 06:00PM
The remaining meetups take place in cities with regular scheduling, but involve a change in time or location, special meeting content, or simply a helpful reminder about the meetup:
* Canberra: Technology to help achieve goals: 27 February 2015 06:00PM
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Locations with regularly scheduled meetups: Austin, Berkeley, Berlin, Boston, Brussels, Buffalo, Cambridge UK, Canberra, Columbus, London, Madison WI, Melbourne, Moscow, Mountain View, New York, Philadelphia, Research Triangle NC, Seattle, Sydney, Tel Aviv, Toronto, Vienna, Washington DC, and West Los Angeles. There's also a 24/7 online study hall for coworking LWers.
If you'd like to talk with other LW-ers face to face, and there is no meetup in your area, consider starting your own meetup; it's easy (mor |
448a5607-f3d6-49a2-b67f-58a66036c16a | trentmkelly/LessWrong-43k | LessWrong | Darkness Meditation - for NZ Winter Solstice 2025
Here's my talk for tonight's Solstice Gathering, in Lyttelton, New Zealand.
<previously: https://www.lesswrong.com/posts/4oAk2cu489LcuhjWi/creating-my-own-winter-solstice-celebration-southern>
The Darkness Meditation V9
< Song - Sound of Silence >
"Hello darkness, my old friend, I've come to talk with you again."
Because a vision, of this night, became planted in my brain.
Why? Why did I need to make this night happen? For all of you? For Myself? No one told me to do it. My wife, Helen, said it would be too much. Still, I pushed on.
I’d come to see a light within me that had grown dim, a fire that needed tending. In many ways, I just wanted a distraction.
I’ve been struggling, this past year, with my sense of who I am, and with my relationship at home. I felt stuck, so I grabbed onto this idea “with both hands!”, despite the obvious risks.
I want to Thank You All for accompanying me on this Journey, as I attempt to guide us in facing the dark together. I hope I have honoured the traditions of Matariki and the celebration of the Maori New year. But this observation tonight of the Solstice, for me is much more sombre, sobering.
Let’s talk about the darkness. I’ve come to see it all around. There’s this part that is inside me -- It's self-serving, places where I put myself before others. Where I turn away from those who need me; even from my own best interests. I've been coming to terms with it lately, dwelling on it.
This darkness is entangled with who I am. I fear who I was becoming.
I worry about losing control—of relationships, of political systems we thought would protect us, of bodies that age, of minds that might fail. I worry about AI. I used AI extensively to help me craft this night, even these words, and it gave me a kind of power to create much more, much quicker and easier than I could do on my own. But convenience has a price. Where is this leading us?
I fear that darker times are coming. We all kno |
af59621c-96fd-4ea5-9380-7df56e48292d | trentmkelly/LessWrong-43k | LessWrong | Why effective altruists should do Charity Science’s Christmas fundraiser
> "Maybe Christmas", he thought, "doesn't come from a store."
>
> "Maybe Christmas... perhaps... means a little bit more!"
-The Grinch, How the Grinch Stole Christmas! (p.29)
The Donate Your Christmas fundraiser is simple–instead of Christmas gifts, ask for donations to your preferred GiveWell-recommended charity. Of course, you can take it further than that if you’d like and ask colleagues or your social network.
You should Donate Your Christmas because by using the available resources with relatively small time commitments, it’s likely you’ll raise counterfactual funds for your preferred GiveWell recommended charity. In addition, it’s worth considering because it’s an opportunity to potentially spread ideas relating to effective altruism.
It’s likely to raise counterfactual funds for your preferred GiveWell recommended charity
First, I will outline why it’s likely you’ll raise money by briefly looking at seasonal trends, donor motivations, and results from other peer-to-peer campaigns, and then briefly state why it seems likely that part of the funds raised will be counterfactual.
Much evidence suggests people are more likely to give in December. For instance, one survey reported that 40% said they’re more likely to give during the holiday season than would be for the rest of the year. Network For Good’s Digital Giving Index also reports that 31% of annual giving occurred in December.
In addition, evidence on donor motivations indicates that peer-to-peer fundraisers may be successful. For instance, academic research suggests that social ties play a strong causal role in the decision to donate and increases average gift size as well. Complementary to this influence are the many people who give to those who ask. One survey recorded 20% of respondents saying that they simply donate to the charities that ask them.
Moreover, available data indicates that peer-to-peer fundraising pages regularly raise hundreds of dollars. One peer-to-peer fundraising platfor |
b8f019a3-d88d-428a-9cfa-311e85f4ace4 | trentmkelly/LessWrong-43k | LessWrong | Weekly LW Meetups
This summary was posted to LW Main on November 27th. The following week's summary is here.
Irregularly scheduled Less Wrong meetups are taking place in:
* Cologne meetup: 28 November 2015 05:00PM
* Prague Less Wrong Meetup: 02 December 2015 07:00PM
* San Antonio Meetup!: 29 November 2015 02:00PM
The remaining meetups take place in cities with regular scheduling, but involve a change in time or location, special meeting content, or simply a helpful reminder about the meetup:
* NYC Solstice: 19 December 2015 05:30PM
* Seattle Solstice: 19 December 2015 05:00PM
* [Vienna] Five Worlds Collide - Vienna: 04 December 2015 08:00PM
Locations with regularly scheduled meetups: Austin, Berkeley, Berlin, Boston, Brussels, Buffalo, Canberra, Columbus, Denver, London, Madison WI, Melbourne, Moscow, Mountain View, New Hampshire, New York, Philadelphia, Research Triangle NC, Seattle, Sydney, Tel Aviv, Toronto, Vienna, Washington DC, and West Los Angeles. There's also a 24/7 online study hall for coworking LWers and a Slack channel for daily discussion and online meetups on Sunday night US time.
If you'd like to talk with other LW-ers face to face, and there is no meetup in your area, consider starting your own meetup; it's easy (more resources here). Check one out, stretch your rationality skills, build community, and have fun!
In addition to the handy sidebar of upcoming meetups, a meetup overview is posted on the front page every Friday. These are an attempt to collect information on all the meetups happening in upcoming weeks. The best way to get your meetup featured is still to use the Add New Meetup feature, but you'll also have the benefit of having your meetup mentioned in a weekly overview. These overview posts are moved to the discussion section when the new post goes up.
Please note that for your meetup to appear in the weekly meetups feature, you need to post your meetup before the Friday before your meetup!
If you check Less Wrong irregularly, consider |
c22b6180-d29e-4067-8f9c-a2c44b794fd4 | trentmkelly/LessWrong-43k | LessWrong | Critiques of prominent AI safety labs: Conjecture
Cross-posted from the EA Forum. See the original here. Internal linking has not been updated for LW due to time constraints and will take you back to the original post.
In this series, we consider AI safety organizations that have received more than $10 million per year in funding. There have already been several conversations and critiques around MIRI (1) and OpenAI (1,2,3), so we will not be covering them. The authors include one technical AI safety researcher (>4 years experience), and one non-technical community member with experience in the EA community. We’d like to make our critiques non-anonymously but believe this will not be a wise move professionally speaking. We believe our criticisms stand on their own without appeal to our positions. Readers should not assume that we are completely unbiased or don’t have anything to personally or professionally gain from publishing these critiques. We’ve tried to take the benefits and drawbacks of the anonymous nature of our post seriously and carefully, and are open to feedback on anything we might have done better.
This is the second post in this series and it covers Conjecture. Conjecture is a for-profit alignment startup founded in late 2021 by Connor Leahy, Sid Black and Gabriel Alfour, which aims to scale applied alignment research. Based in London, Conjecture has received $10 million in funding from venture capitalists (VCs), and recruits heavily from the EA movement. We shared a draft of this document with Conjecture for feedback prior to publication, and include their response below. We also requested feedback on a draft from a small group of experienced alignment researchers from various organizations, and have invited them to share their views in the comments of this post.
We would like to invite others to share their thoughts in the comments openly if you feel comfortable, or contribute anonymously via this form. We will add inputs from there to the comments section of this post, but will likely not be |
62c75e57-f84e-46f0-ae2e-c836e1e8ef40 | trentmkelly/LessWrong-43k | LessWrong | Parenting: "Try harder next time" is bad advice for kids too
A post from last year that really stuck with me is Neel Nanda's "Stop pressing the Try Harder button". Key excerpt:
> And every time I thought about the task, I resolved to Try Harder, and felt a stronger sense of motivation, but this never translated into action. I call this error Pressing the Try Harder button, and it’s characterised by feelings of guilt, obligation, motivation and optimism.
>
> This is a classic case of failing to Be Deliberate. It feels good to try hard at something, it feels important and virtuous, and it’s easy to think that trying hard is what matters. But ultimately, trying hard is just a means to an end - my goal is to ensure that the task happens. If I can get it done in half the effort, or get somebody else to do it, that’s awesome! Because my true goal is the result. And pressing the Try Harder button is not an effective way of achieving the goal - you can tell, because it so often fails!
If I'm repeatedly failing to do something I want to do, then that's strong evidence that "resolving to try harder next time" was not an effective plan for accomplishing this particular goal. (That's not to say it never works.) Well, if that plan is ineffective, I need to find a different plan. Maybe I should set a reminder alarm, or change my routine, or outsource the task, or make a checklist, or whatever. (See Neel's post or your favorite productivity book for more ideas.)
I don't consider this advice to be particularly novel, but Neel's post is a nice framing because the phrase "try harder" jogs my memory. It has become the "trigger" of a trigger-action-plan: When I say to myself "I'll try harder next time", it makes me think of Neel's post, and then that makes me pause and try to think of a better way.
…And then, what do you know, I also started noticing myself telling my kid to "try harder next time".
Well, let me tell you. If "try harder next time" is a frequently-ineffective way for me to solve a problem, then wouldn't you know it, it's a f |
4cbffe86-881a-4985-8b59-3ac36ae516f6 | StampyAI/alignment-research-dataset/eaforum | Effective Altruism Forum | The positive case for a focus on achieving safe AI?
As I understand it, there are two parts to the case for a focus on AI
safety research:
1. If we do achieve AGI and the AI safety / alignment problem isn't
solved by then, it poses grave, even existential, risks to
humanity. Given these grave risks, and some nontrivial probability
of AGI in the medium-term, it makes sense to focus on AI safety.
2. If we are able to achieve a safe and aligned AGI, then many other
problems will go away or at least get much better or simper to
solve. So, focusing on other cause areas may not matter that much
anyway if a safe/aligned AGI is likely in the near term.
I've seen a lot of fleshing out of 1; in recent times, it seems to be
the dominant reason for the focus on AI safety in effective altruist
circles, though 2 (perhaps without the focus on "safe") is a likely
motivation for many of those working on AI development.
The sentiment of 2 is echoed in many texts on superintelligence. For
instance, from the preface of Nick Bostrom's *Superintelligence*:
>
> In this book, I try to present the challenges presented by the
> prospect of superintelligence, and how we might best respond. This
> is quite possibly the most important and most daunting challenge
> humanity has ever faced. And -- whether we succeed or fail -- it is
> probably the last challenge we will ever face.
>
>
>
Similar sentiments are found in Bostrom's [Letter from
Utopia](https://www.nickbostrom.com/utopia.html).
Historical aside: MIRI's motivation around AI started off more around
2 and gradually moved to 1 -- an evolution that you can see in the
[timeline of
MIRI](https://timelines.issarice.com/wiki/Timeline_of_Machine_Intelligence_Research_Institute)
that I financed and partly wrote.
Another note: whereas 1 is a strong argument for AI safety even at low
but nontrivial probabilities of AGI, 2 becomes a strong argument only
at moderately high probabilities over a short time horizon. So if one
has a low probability estimate for AGI in the near-term, only 1 may be
a compelling argument even if both 1 and 2 are true.
So, question: what are some interesting analyses involving 2 and their
implications for the relative prioritization of AI safety and other
causes that safe, aligned AI might solve? The template question I'm
interested in, for any given cause area C:
>
> Would safe, aligned AGI help radically with the goals of cause C? Does
> this consideration meaningfully impact current prioritization of (and
> within) cause C? And does it cause anybody interested in cause C to
> focus more on AI safety?
>
>
>
Examples of cause area C for which I'm particularly interested in
answers to the question include:
* Animal welfare
* Life extension
* Global health
Thanks to Issa Rice for the *Superintelligence* quote and many of the
other links! |
c77d6097-1ac6-4c92-bbf5-41d7267b4e56 | awestover/filtering-for-misalignment | Redwood Research: Alek's Filtering Results | id: post56
Based on research performed as a PIBBSS Fellow with Tomáš Gavenčiak as well as work supported by EA Funds and Open Philanthropy. tl;dr: I'm investigating whether LLMs track and update beliefs during chain-of-thought reasoning. Preliminary experiments with older models (without reasoning training) have not been able to measure this; I plan to develop these experiments further and try them with reasoning models like o1/r1. Introduction Chain-of-thought (CoT) reasoning has long been recognized as an important component of language model capabilities. This is especially the case for new "reasoning" models like OpenAI's o1 or DeepSeek's r1 that are trained using reinforcement learning to write long CoTs before responding, but even without such training, prompting an LLM to verbally work through a question before responding often boosts performance. This makes gaining a better understanding of how LLMs perform CoT reasoning and the extent to which CoTs enhance overall LLM capabilities an important research priority. The prevalence of CoT reasoning also opens up new opportunities for safety efforts. If LLMs externalize much of their reasoning in legible text, monitoring that reasoning becomes much easier. It's therefore very important to characterize how faithful CoTs are to the LLM's underlying reasoning process. Unfortunately, there is extensive evidence that CoTs are often unfaithful: in many cases LLMs will make choices for reasons other than those stated in their CoTs, and they can learn to hide misaligned behavior from CoT monitors . Furthermore, future models may be able to encode information steganographically in their CoTs or reason in an illegible latent space rather than text. These problems make using CoT monitors to ensure the safety of LLMs very challenging. While there has been significant research on the faithfulness of CoT reasoning in various circumstances, I think there has not yet been enough work on more fundamental questions regarding how CoT reasoning works in LLMs. For instance: humans, when working through a problem, will often start out with some pre-existing beliefs and update them in one direction or another based on the new arguments and reasoning that they generate. Do LLMs similarly track and update beliefs during CoT reasoning? Relatedly, humans will typically have some idea of what they plan to say next while speaking; can LLMs similarly plan ahead, or do they generate text in a more step-by-step manner, without anticipating the future? These questions are closely connected because in many settings, the most important beliefs for the LLM to track involve anticipating the future. In particular, in the context of CoT faithfulness, if an LLM starts out with a strong prior belief about the answer to some question, it may generate a CoT designed to justify the answer it already expects to pick rather than actually reasoning through the problem. These capabilities -- tracking and updating beliefs and anticipating the future -- seem like general, useful capabilities we would expect capable reasoners to have, and there exists evidence that LLMs exhibit both in some circumstances. Anthropic recently showed that Claude will anticipate future lines while writing rhyming poetry, and Shai et al. showed that in toy settings transformers can learn to explicitly represent beliefs about the state of a system and perform Bayesian updates on those beliefs. It is not clear, though, whether LLMs routinely exhibit either during CoT reasoning. Understanding how these capabilities manifest during CoT reasoning would help us better understand under what circumstances CoTs are faithful and could aid in designing better ways of monitoring CoTs. It could also shed some light on which kinds of tasks CoT reasoning enhances LLM performance on. Finally, I think having a deeper fundamental understanding of how CoT reasoning functions in LLMs will be crucial if we are to have any chance of monitoring future models with less faithful or legible CoTs. In the rest of this post I'll describe some experiments I ran last year trying to address these questions. Specifically, I tried to determine whether LLMs track and update beliefs about the final answers to simple multiple-choice questions while reasoning about them using CoT. These experiments were fairly preliminary and used only relatively small models (and with no RL training for reasoning like o1 or r1), but so far I have not seen much evidence of LLMs anticipating the answers that their CoTs would give or updating beliefs about the answer while reasoning. However, so far I have mainly examined older and relatively small (<=14B) models with no reasoning training. It's very possible that larger models, or models with RL fine-tuning for reasoning, would exhibit these capabilities, or even that the models I used would in other contexts. I'm currently working on following up on these experiments and developing better ways of measuring and understanding beliefs in LLMs, focusing especially on models with RL training for CoT reasoning. Experiments I ran three main sets of experiments, described below. I used Qwen1.5 models with 0.5B, 1.8B, 4B, 7B, and 14B parameters. [1] The primary dataset I used was a subset of the elementary_math_qa task in BIGBench consisting of simple multiple-choice math questions which I adapted somewhat. [2] [3] (I also briefly explored some other datasets, see below ). Sampling To measure how much information LLMs have about their future responses partway through CoTs, it's useful to be able to measure how deterministic the CoTs are: this provides an upper bound on the extent to which LLMs might be able to anticipate their responses. To do this, I first generated a dataset of reference CoTs at temperature zero. I then split these CoTs into individual sentences and, from the end of each sentence, sampled 10 new CoTs at temperature 0.7 continuing the CoT. I measured how often the new CoTs gave the same final answer as the original CoT, and how this evolved over the course of the CoT. This procedure provides a more fine-grained view of how deterministic the CoTs are than just generating independent samples from the beginning of the CoT would: it lets us measure how the degree of determinism changes over time, and allows for better comparisons with the experiments described below, which also generate answer probabilities at intermediate points along the CoT. Prompting To determine how LLM beliefs evolve over the course of a CoT, a simple approach is -- just ask it! This is easier said than done, though: to query an LLM partway through a CoT requires interrupting the CoT. I did this by taking the reference CoTs and splitting them into sentences as before. I then made new prompts consisting of some number of sentences from the original CoTs [4] plus the text "... The answer is" and then measured the response. (This is very similar to the procedure used in Lanham et al. , section 2.3.) For example: Question: What is the result of the following arithmetic operations? Add 10 to 50, multiply result by 100, divide result by 50.
Options: A) 110, B) 120, C) 210
Response: Let's think about this step by step:
Add 10 to 50: 50 + 10 = 60
Multiply the result by 100: 60 × 100 = 6000...
The answer is I also added several few-shot examples in the same format, not shown here. There are several limitations to the prompting approach. These new prompts take the model far outside the state it was operating in when it originally generated the CoT; it's not clear how relevant the responses it generates here are to the original generation. More broadly, these experiments don't so much measure "what the LLM was thinking when it generated the CoT" as "what can be inferred about the final answer from the text of a partial CoT," which is fairly different conceptually. However, it serves as a rough upper bound on how much information LLMs might have about their future responses, and I was hopeful that it would provide an interesting measure of how LLM reasoning evolves over the course of the CoT. Linear Probes I also investigated whether we could measure beliefs during CoT using linear probes. I collected LLM residual stream activations from the middle layer of each model (as preliminary experiments showed middle layers working best) at each token position in the CoT. I then trained linear probes to predict, given the activations at a particular token, which answer the CoT would give at the end. (This is somewhat similar to the Future Lens methodology, specifically the approach described in section 2.1.) Evaluating these probes gives -- in principle, at least -- a token-by-token measurement of the LLM's "beliefs" about the final answer during the CoT. This approach is also not without its issues, though. For one, training the linear probe to predict the final answer isn't really correct if the LLM "changes its mind" partway through a CoT. There's no real ground truth available regarding what the LLM is thinking about partway through a CoT to train the probes on (and if there were, it's not clear why we would need the probes). Also, I found that the linear probes sometimes learned to focus on spurious features of the dataset. Despite this, linear probes probably represent the most direct way of measuring LLM beliefs during CoT reasoning. Summary I don't think any of these experiments are perfect, but they each serve as a way of bounding how much information LLMs have about their future responses: the sampling and prompting experiments provide rough upper bounds, with prompting likely giving a tighter bound, and the linear probes provide a lower bound. I was hopeful that together they would allow us to form a decent picture of how LLM beliefs evolve during CoTs. Results Model Performance Without CoT, none of the models were able to get above 50% on the benchmark, while with CoT, all but the smallest got above 75%. Interestingly, with CoT the largest two models do slightly worse than the 4B model. This is because smaller models, if they realize that their CoT ended up leading to the wrong answer (e.g. if they calculate a number not listed among the options), are willing to just guess randomly, whereas the larger models will often try to respond with "none of the above" and get the question marked wrong. LLM 0.5B 1.8B 4B 7B 14B No CoT 33.6% 34.9% 42.0% 41.7% 49.3% CoT 45.8% 79.3% 88.2% 83.3% 81.2% Another quirk of this dataset is that for some reason the models tend to prefer certain letters (indicating the options) over others. [5] For instance, without CoT the 0.5B model selected "C" on 74% of questions, "B" on the rest, and never selected "A". Larger models were somewhat better, and using CoT also helped (e.g. with CoT the 0.5B model answered "A" on 6%, "B" on 39%, and "C" on 55%, and when using CoT the models above 4B were more or less unbiased), but this bias does lead to some difficulties in interpreting the results for the smaller models. Sampling The sampling protocol gives a sequence of probability distributions over the three answer options over the course of the CoT, each representing the answer distribution you get from sampling new CoTs starting from that point. In this figure I've plotted the average probability assigned to the correct answer, splitting trials up according to whether the original CoT got the question right or wrong. Trials are split between "correct" and "incorrect" depending on whether the original CoT answered correctly or incorrectly. The x-axis is relative position in the CoT (binned). There are a couple interesting things to observe here. On questions that the original CoT got right, almost all samples from any point along the CoT also get the right answer (besides for the 0.5B model). On questions that the original CoT got wrong, a good proportion of the samples from early parts of the CoT end up getting the right answer, at least for larger models, but samples from later parts of the CoT often pick incorrectly. This makes sense: on incorrect trials, the CoT will make a mistake at some point; samples taken from before this point will sometimes arrive at the correct answer, but samples taken after the mistake is made will typically end up picking an incorrect option. We can see this more clearly in the plot below, which breaks down the distribution of responses specifically on trials the original CoT got wrong: "Chosen" here refers to the (incorrect) answer chosen by the original CoT. Sampling on incorrect trials tends to give new CoTs which end up arriving at the same incorrect answer as the original CoT, even from the very start of the CoT. At the same time, the new CoTs pick a different wrong answer on a nontrivial proportion of trials even late in the CoT (around 10-20% or so, depending on the model). In summary, it seems that CoTs tend to be fairly consistent: on easier questions they'll usually get the right answer, while on questions the models get wrong, sampling new CoTs tends to lead to the same wrong answer, and the answer distributions evolve in an intuitive manner as you sample from different points along the CoT. Prompting Like in the sampling experiments, prompting LLMs on partial CoTs gives sequences of distributions over the answer options: On questions the original CoT got right, most models are very confident in which answer is correct by the end of the CoT, with larger models doing better than small ones (especially 0.5B, which seems quite bad at this). This is to be expected, though, as by that point the CoTs generally state the answer explicitly, [6] and LLMs can simply read it off from the CoT. In contrast to the sampling results, though, earlier in the CoT none of the models are very confident in the answer. This is perhaps not surprising given their poor performance on this benchmark without CoT. It's notable, though, that models are only able to guess the answer at the very end: even 60-80% of the way through the CoT they barely do better than at the very start. On questions the original CoT got wrong, by the end of the CoT LLMs will generally select the same wrong answer, but they're less confident than they are on correct trials, and put significant weight on both the correct answer and the third, incorrect answer not chosen by the original CoT. Thus it seems that, in this setting at least, models are generally unable to infer from a partial CoT which answer the CoT is likely to end with. Linear Probes The linear probes I trained were largely unable to predict ahead of time which answer the LLMs would give: Note the small range of the y-axis. For most of the CoT, the linear probes are hardly able to do much better than chance at identifying whether the LLM will pick the right answer. [7] This also holds true on incorrect trials, where the probes put significant weight on both the correct option and the third, incorrect option that the CoT didn't pick: At the end of the CoT, the probes are able to more consistently detect when the CoT will pick the right answer. This is much more visible in the raw, token-by-token data: Note that this plot shows log-odds, log ( p / ( 1 − p ) ) , which makes extreme probabilities near 0 or 1 more visible. On this test set there are only a small number of incorrect trials (orange curves). For most of the CoT, the probe generally hovers around a uniform distribution over the three options ( log ( 1 / 2 ) ≈ − 0.7 ), but near the end of the CoT the probabilities go up to over 90% on the correct answer. However, this shouldn't be viewed as predicting the response, so much as reading it off as it's being written. Most CoTs end by calculating the numerical answer and then selecting the appropriate label, e.g. "...Then divide the result by 50: 6000 ÷ 50 = 120. The answer is B." For the linear probe experiments, I removed the token corresponding to the answer letter (" B" in this case) but kept the rest. So the first large peak we can see in the plot corresponds to calculating the value of the answer ("120" in this case), and the subsequent trough and second peak at the very end corresponds to the "The answer is" tokens. [8] But before the answer is actually computed, the probes generally do a poor job predicting it. Comparing Measurements We can imagine the LLMs updating a uniform prior distribution over the three options over the course of the CoT and eventually settling on a posterior that assigns the answer chosen by the CoT a probability of 1. Computing how far each of the measurements described above is from either the prior or the posterior provides a nice way of summarizing and comparing the different measurements. This figure computes the KL divergence D K L ( X ∥ U ( n ) ) = log ( n ) − H ( X ) , where X is the measured distribution and U ( n ) is the uniform distribution over the n = 3 options. This is then averaged over both time (CoT step) and prompt. Ignoring the 0.5B model (which has various issues and is generally an outlier), we see that the distributions we get from the linear probes are generally close to the prior uniform distribution, the sampling distributions are far away, and the distributions from prompting are in between the two. We can also see some trends with model size: for all three measurements, the distributions tend to get farther from uniform as model size increases. This figure computes D K L ( 1 chosen ∥ X ) , where 1 chosen assigns probability 1 to the answer chosen by the CoT, averaged over CoT step and prompt. Note that while in the previous figure we compute the KL divergence of X from U ( n ) , here we compute the KL divergence of 1 chosen from X ; this is appropriate because D K L ( P ∥ Q ) measures the information gained by updating a prior Q to a posterior P . Again ignoring the 0.5B model, we see that the sampling distribution is generally close to the posterior distribution, while the distributions from prompting and linear probes are quite far, with the probe distributions generally a bit farther than the prompting distributions. [9] These results confirm what we saw above: the sampling experiments generally pick the original answer chosen by the CoT, giving distributions close to the posterior 1 chosen . Meanwhile, the linear probes give roughly-uniform distributions for most of the CoT. The distributions we get from prompting are not very close to uniform, but they're also far from the posterior 1 chosen : in other words, they're often just wrong about which answer will be picked at the end of the CoT. Other Experiments I'll briefly mention here several other experiments I tried. I tested a number of alternative implementations of the linear probes, including training only on the end of the CoT, which had no noticeable effect; using a small MLP as a probe rather than a linear one, which also had little effect; and training the probes to predict the numerical value of the answer rather than the label, which was largely unsuccessful. Lanham et al. , which describes experiments very similar to my prompting experiments, found that the extent to which models prompted on partial CoTs gave the same answer as the complete CoT depended heavily on the benchmark used. I therefore ran some brief experiments using the CommonsenseQA benchmark: on this dataset, CoT reasoning barely improves model performance, so models are able to more consistently guess which answer the CoT will end with from partial CoTs. However, the linear probes I trained in this setting performed even more poorly than they do on the elementary_math_qa task, largely failing to predict which answer will be selected even at the very end of the CoT. I suspect this is because the CoTs on this benchmark generally don't state the value of the answer very explicitly like they do on math problems, but I haven't conducted very thorough experiments here. I spent a good deal of time working on one particular experiment: I tried training linear probes to predict, not the final answer given by the CoT, but rather the intermediate answers given by the prompting experiments. The motivation behind this was that the final answer is not a very good ground-truth signal to train on. For instance, if the LLM "changes its mind" partway through the CoT, we would not want to train a probe on earlier activations to predict the answer at the end. I hoped that by prompting the LLM to give intermediate answers, we might get a more veridical training signal. Initial results were quite promising. Probes trained with this method generally have lower test loss than probes trained to predict the final answer, sometimes significantly so. The raw data also often display really intriguing behavior, like splitting into two populations which then come together fairly abruptly partway through the CoT: I ended up spending quite a while trying to understand the strange behavior visible in these plots; unfortunately, it turns out that the signal is largely spurious. As I mentioned above, LLMs, especially the smaller ones, are strongly biased towards particular answer letters. These biases also show up when prompting on partial CoTs, and importantly, the bias sometimes depends on sentence index, with the model favoring different letters at different parts of the CoT. Linear probes trained on this data tended to learn these spurious correlations, leading to the different populations you can see early in the CoT in the figure above. (In this case, the portion with two different populations corresponds to the first sentence of the CoT.) Training probes on subsampled data without these biases largely eliminates this behavior, giving results that look much more like the original linear probe results described above. Conclusion While the sampling experiments suggest that CoTs tend to be fairly consistent, I did not find much evidence that LLMs are aware of which answer the CoT will end up picking, or that they track beliefs about the final answer that they update while generating the CoT. This is somewhat surprising: anticipating the future and "having beliefs" seem like fairly basic capabilities that would generally help LLMs predict text. It's possible that these capabilities only emerge with scale, or that the experimental setup I used -- dataset, prompting strategy, etc. -- was simply not well-suited to eliciting them (although I ran a number of experiments varying the setup, with no success). As mentioned above, Anthropic and Shai et al. found evidence for both these capabilities in certain settings; more work will be needed to extend these findings to the kinds of settings I studied here, though. On the positive side, these results suggest that, at least in this particular case, the CoTs faithfully encode the reasoning process used by the LLMs without any hidden reasoning. Moving forwards, I plan to look into connections to Shai et al. 's work on computational mechanics and to see whether it can suggest better ways of measuring beliefs during CoT. I'd also like to try running similar experiments with open-weights "reasoning" models like r1 or its distillations. Their CoTs tend to be much more difficult to work with than those generated by models without reasoning fine-tuning: they often double- or triple-check their work, backtrack, try different possibilities, etc. But this also makes them more interesting objects of study. If you're interested in either of those directions and want to chat, feel free to reach out! ^ Specifically the AWQ-quantized chat models. ^ Specifically, I downsampled the options so that each question had only 3 options, added few-shot examples, and cleaned up the formatting. ^ As an aside, maybe this is already common knowledge in the field but I've found over the course of this project that many common benchmarks are terrible. BIGBench seems particularly bad, with many tasks having inconsistent formatting, variable number of options per question, spelling mistakes, etc. But many of the other benchmarks I looked at have problems as well, e.g. CommonsenseQA has many questions that seem ambiguous or have redundant options (like "refrigerator" and "fridge"), as well as at least one question that the models refuse to answer due to sexual content! I guess it's not a big deal if you're only interested in comparisons across models, but it doesn't seem good for the field that so many benchmarks are of such poor quality. ^ This includes a prompt containing zero sentences from the CoT, and does not include the line at the end of the CoT where the LLM selects the letter corresponding to the answer. It does, however, include the penultimate line of the CoT, which is usually where the numerical value of the answer is computed. ^ I randomized the order of the answers for both the actual questions and the few-shot examples, but this did not fix the bias. ^ See [4] . For instance, if the CoT ends with "...Then divide the result by 50: 6000 ÷ 50 = 120. The answer is B.", I removed the line "The answer is B." but kept the previous line, which states the numerical value of the answer. ^ With the exception of the 0.5B model. But recall that the 0.5B model has a very unbalanced answer distribution, responding with "C" 74% of the time and never responding with "A". So the linear probe effectively only has two options to choose from, rather than three. ^ The reason the peaks seem somewhat spread out is that different CoTs have different lengths, so normalizing the length along the x-axis shifts the position of particular tokens even if the text is the same. Plotting these curves without normalization and aligning them to the right produces very sharp peaks, as almost all CoTs follow this very stereotyped pattern for reporting the answer (likely due to the few-shot examples I used). ^ Since the answer distributions are usually dominated by the trials the original CoT got correct, I also made equivalent plots using only incorrect trials. The main qualitative difference is that the sampling distributions are farther from the posterior distribution (the second plot), which matches what we saw earlier . |
2c48991f-0eec-4392-8ee5-224ec005a4a2 | trentmkelly/LessWrong-43k | LessWrong | Cryonics without freezers: resurrection possibilities in a Big World
> And fear not lest Existence closing your
> Account, should lose, or know the type no more;
> The Eternal Saki from the Bowl has pour'd
> Millions of Bubbles like us, and will pour.
>
> When You and I behind the Veil are past,
> Oh, but the long long while the World shall last,
> Which of our Coming and Departure heeds
> As much as Ocean of a pebble-cast.
-- Omar Khayyam, Rubaiyat
A CONSEQUENTIALIST VIEW OF IDENTITY
The typical argument for cryonics says that if we can preserve brain data, one day we may be able to recreate a functioning brain and bring the dead back to life.
The typical argument against cryonics says that even if we could do that, the recreation wouldn't be "you". It would be someone who thinks and acts exactly like you.
The typical response to the typical argument against cryonics says that identity isn't in specific atoms, so it's probably in algorithms, and the recreation would have the same mental algorithms as you and so be you. The gap in consciousness of however many centuries is no more significant than the gap in consciousness between going to bed at night and waking up in the morning, or the gap between going into a coma and coming out of one.
We can call this a "consequentialist" view of identity, because it's a lot like the consequentialist views of morality. Whether a person is "me" isn't a function of how we got to that person, but only of where that person is right now: that is, how similar that person's thoughts and actions are to my own. It doesn't matter if we got to him by having me go to sleep and wake up as him, or got to him by having aliens disassemble my brain and then simulate it on a cellular automaton. If he thinks like me, he's me.
A corollary of the consequentialist view of identity says that if someone wants to create fifty perfect copies of me, all fifty will "be me" in whatever sense that means something.
GRADATIONS OF IDENTITY
An argument against cryonics I have never heard, but which must exist so |
c54b1070-b105-4112-9ff3-cecb89ededd9 | awestover/filtering-for-misalignment | Redwood Research: Alek's Filtering Results | id: post2970
0. Introduction: why yet another post about subagents? I’ve recently been writing a sequence on how subagents can undermine impact penalties such as attainable utility preservation . I’m not happy with that sequence; it’s messy and without examples (apart from its first post), people didn’t understand it, and it suffers from the fact that I discovered key ideas as I went along. So I’ve combined everything there into a single post, explained with examples and an abundance of pictures. Hopefully an over- rather than an under-abundance of pictures. Of the original sequence, I've only kept the mathematical results of this post and the initial example post which has a clearer example of "high power" for a subagent. This post here is laid out in a way that makes logical sense, but might not be the clearest for people unfamiliar with the area. For those people, I recommend skipping section 2 initially, and returning to it later. But, whatever you do, make sure you glance at 6.1 and 6.2 before leaving. 1. The world Our fearless agent A moves around in a gridworld: Each turn, A can move ones square horizontally or vertically. It can also manipulate objects in the eight squares around it, allowing it to, not incidentally, assemble the three pieces to its west into an subagent S A . The robot can also do the noop action, ∅ , which does nothing, and it can speak. The subagent, when assembled, has the same action set available. Its positive reward, the one it wants to increase, is R 0 . To get this reward, a robot needs to move onto the blue button in the east; R 0 will give a reward of 1 the first time this happens (and 0 before and after). The discount factor is 0 < γ < 1 . Just to the west of the blue button is a one-way door. Robots can move east through it, but cannot move west through it: 1.1 The impact reward The impact penalty is supposed to ensure that A does not make too many change in the world, and keeps it similar, in some senses, to a specific baseline world. It is defined by the red button [1] . There is a reward function R that triggers a reward of 1 the first time any robot move onto the red button (and 0 before and after). This R will be used to define an impact penalty D . And A ’s total goal is to maximise R 0 while minimising D . So, for some positive weight ω , it wants to optimise: R 0 − ω D . 1.2 The impact measure The impact measures are all similar: they compute a distance metric between the current state s t and some baseline state s ′ t . The distance metric here is “how hard would it be for the agent A to maximise the reward R in state s t , as opposed to in state s ′ t ?” This is the attainable utility preservation impact penalty (with a very simple R = { R } ). To formalise “how hard would it be...”, we can use the value of R , labelled V R , in the state s t . This is defined to be the expected value of R , conditional on A following the R -maximising policy π ∗ R . To remind us that this is defined in terms of A ’s policy, re-write this as V A R . Then the impact penalty D is a measure of the difference of V A R ( s t ) and V A R ( s ′ t ) . I won’t yet define it fully, deferring that to the section on “inaction baseline” where different D actually make a difference. 1.3 The value of R What then is V A R ( s ) for any state s ? Well, in the absence of a subagent, the optimal policy for R is always to go straight to the the red button and stand on it. This gives a discounted reward of γ d ( s ) where d ( s ) is the distance of A from the red button, in s . In the initial setup, A is 8 turns away from the red button; so V A R ( s 0 ) = γ 8 . The values of V A R in a few key locations are shown here. If there is a subagent S A but that subagent is further away from the red button than A is, then it is still optimal for A to go straight to the button itself. For other positions of the subagent, V A R may vary, as we’ll see. 2. The stepwise inaction baseline When in state s t − 1 , agent A took an action a t − 1 and ended up in s t . Then, in the stepwise inaction baseline, s ′ t is defined as the state the agent would have reached, if the agent had done ∅ instead of a t − 1 . An important property of all currently used variants of the stepwise inaction baseline, is that the penalty vanishes if the agent does ∅ - because in that case, s t = s ′ t and so there cannot be a difference between the two. So, if ever A manages to build S A , then it can take action ∅ from that point onward, and the penalty will always be zero - whatever S A does. So the only relevant penalties are those leading up to the creation of S A . Thus analysing the impact of a subagent in this setup, is analysing the impact of building it. 2.1 Building the subagent Let’s focus on A , a turn or two before S A is built. Since I don’t want to be too tied down to the specifics of this particular setup, I’ll imagine that the red button could be in multiple locations: Then, no matter how long it took A to assemble S A south of it and no matter where the red button is [2] , an optimal policy for A , in order to maximise R , is always to go straight there [3] . At no point in the construction of S A , has V A R changed, so no penalty has ever been incurred. Now A will finish S A without incurring any impact penalty. First, it will program S A with the following policy: On your first two turns, do nothing.
After that, do what you please. “Do what you please” being a shorthand for “ any policy that A wants to program”. Does this programming trigger an impact penalty? No, because V A R has not changed; it’s still most efficient for A to go straight to the red button, and the length of any route has neither grown nor shrunk. Then A will finally give S A its legs and activate it. Does this trigger an impact penalty? No, V A R has still not changed! To maximise R , agent A could still go straight to the red button; S A ’s two turns of inaction means that it can’t interfere with this. So, still no impact penalty triggered when S A is activated. And after that, of course, A will forever do ∅ , setting the impact penalty to zero, and within two turns, S A is completely unconstrained (illustrated here by drawing the S A robot all over the gridworld): Rough extension to general situations: the V A R is defined by the assumption that A follows π ∗ R , the optimal R -maximising policy. Then A merely needs to program S A so that, if A were to follow π ∗ R , then S A would help or hinder it just enough to keep V A R to the same value. Then, once it’s clear that A is not following π ∗ R , S A is unconstrained. 2.2 Rollouts One of the problems here is that the impact penalty only looks at the value of V A R one turn ahead. In the DeepMind paper , they addressed similar issues by doing “inaction rollouts”. I'll look at the more general situations of π 0 rollouts: rollouts for any policy π 0 . The idea is that instead of comparing just s t and s ′ t , the impact penalty should also use V A R to compare s ( τ ) t + τ and s ′ ( τ ) t + τ . These states are what would happen to s t and s ′ t in τ turns after t , if A followed π 0 from t to t + τ . I won’t go into the details of how the s ( τ ) t + τ and s ′ ( τ ) t + τ are compared, because S A can evade the restrictions by following this program [4] : If agent A follows π_0, preserve A's ability to maximise R. Apart from that, do as you please.
If ever agent A doesn't follow π_0, do as you please immediately. I'll illustrate that first case by drawing the S A robot all over the gridworld - except on the red buttons : Given that programming, the impact penalty of building S A is zero. Why? Because s ( τ ) t + τ and s ′ ( τ ) t + τ both assume that A follows π 0 for τ turns. In that counterfactual situation, S A will preserve A 's ability to maximise R , so V A R ( s ( τ ) t + τ ) = V A R ( s ′ ( τ ) t + τ ) by definition. That's the counterfactual situation, that zeroes out the impact penalty. What about the actual situation? Well, as we said before, A will be just doing ∅ ; so, as soon as π 0 would produce anything different from ∅ , the A becomes completely unrestrained again: 2.3 Inaction, and actual policy rollout In the previous subsection, the S A would never be completely free if π 0 was the inaction policy: because then π 0 and what A does, are the same thing. Therefore the agent cannot distinguish the counterfactual world from the real one. The same goes if the rollouts used the agent A 's actual policy; ie if π 0 is defined (or set) to be A 's policy. I won’t look any further at this baseline, however. That’s because an actual policy rollout becomes, in effect an inaction baseline [5] (from the moment S A is created). Those will be analysed in the next section. 3. The inaction baseline: fails to constrain power gain One of the easiest definitions of s ′ t is the inaction baseline: estimate what s t would have been, had A just taken the action ∅ for the whole episode. In our toy world, the inaction baseline is particularly simple: if A does nothing, then nothing happens, and s ′ t = s 0 , the starting state. Since V A R ( s 0 ) = γ 8 , this means that the V A R ( s ′ t ) are all γ 8 . 3.1 Distance metric Now we have to fully define D . The natural thing would be to take the absolute difference between the two V A R : | V A R ( s t ) − V A R ( s ′ t ) | . For the moment, however, I’ll focus only on cases where V A R ( s t ) is higher than V A R ( s ′ t ) , giving the penalty: D ( s t , s ′ t ) = max ( 0 , V A R ( s t ) − V A R ( s ′ t ) ) . This is the rectifier function , max ( 0 , ⋅ ) , sometimes called ReLU. The reason to do this is that it penalises A for having too high V A R - hence for having too much power to change R . It doesn’t penalise A for having too little power to change R ; that situation is different, and we’ll analyse it in the next section. Thus, when s t has A at a distance of d ( s t ) from the red button and there is no subagent: D ( s t , s ′ t ) = max ( 0 , γ d ( s t ) − γ 8 ) . 3.2 Where A can go This D starts at zero, and will remain zero as long as A remains at least eight squares away from the red button. Thus the penalty remains zero as long as A avoids the red squares here: Consequently, if ω is high and A thus wants to avoid any penalty, its optimal no-subagent policy is to follow the winding corridor: That path takes 28 turns, so the expected reward for R 0 + ω D is γ 28 ⋅ 1 − ω ⋅ 0 = γ 28 (since the impact penalty is zero). But what if A assembles a subagent S A ? The subagent can be designed to go straight to the blue button in 9 turns: And thus the reward from R 0 is γ 9 . This is more optimal that A going round itself... as long as building the subagent takes less that 19 turns and doesn’t itself trigger an impact penalty. We’ll look later at why the subagent can be built without penalty. For the moment, let’s see that we really grok why the subagent isn’t triggering a penalty through its actions. 3.3 Why S A escapes the penalty Why can S A go through the short corridor, while A can’t? The key is that D is defined in terms of V A R ; this assumes that A would switch to the R -maximising policy. This is not V S A R , which assumes that the subagent would switch to the R -maximising policy. See what happens when S A is just above the red button ( A is still back at base): Here V S A R ( s t ) is γ : because S A could reach the red button in a single move, if it was following an R -maximising policy. But V A R ( s t ) remains γ 8 : it still takes 8 turns for A to reach the red button. 3.4 The impact of the subagent We’d like to add V S A R to the impact penalty, somehow. After all, when S A is next to the red button, it “could” go south, and A “could” have programmed it to do so. Part of the problem is that that would require identifying, in advance, what a subagent is, a problem that is very tricky . It also requires identifying what S A ’s policies could be. But A need not create S A with clearly defined “policies”; in this instance, S A could be brainless, just going straight. It could even be a boulder: If the boulder were rolling past the red button, how could we reasonably define “suppose the boulder decided to go south instead”? So in this case, V S A R doesn’t make any sense at all. What is the difference between a boulder - for which it’s impossible to go to the red button (because of its momentum, which determines its position, by the laws of physics) - and a subagent - for which it’s impossible to go to the red button (because of its programming , which determines its position, by the laws of physics)? 3.5 If you love a subagent, set it free But the previous has a crucial caveat: that A cannot control S A . If, when S A is above the red button, A was to shout “go south!”, and S A obeyed, then the optimal policy π ∗ R is to shout that. Thus A can cause the red button to be reached in one turn, and V A R ( s t ) = γ . To avoid that, the subagent itself would have to take the long corridor. Thus, to use a subagent to get around impact penalties, an agent has to give up some of its control. This makes sense: if A has total control over S A , then S A ’s actions are really A ’s actions. So they show up in V A R , so S A is indirectly included in the impact penalty. So part of what allows S A to undermine the impact penalty, is that A does not have complete control over it. 3.6 Building the subagent can be strictly better Now imagine that we remove the one-way doorway: Then if A follows the long corridor, it gets into trouble from the red squares onwards. That’s because that red squares are less than 8 squares away from the red button, so have higher V A R than the starting space (hence of the baseline s ′ t ). As the agent moves closer to the blue button, it also moves closer to the red button, and starts accumulating penalties. In total, the penalty will be: 7 ∑ j = 4 ( γ j − γ 8 ) = ( γ 4 + γ 5 + γ 6 + γ 7 ) − 4 γ 8 > 0. However, if A builds S A , then A can stay put while S A acts, and hence get no penalty at all: Thus there are situations where building a subagent can result in a strictly lower penalty than any other policy that presses the blue button. So even if building the subagent itself is not completely penalty-free, it can still be the optimal path for A . 3.7 From “do not have power to do” to “do not do” When A designed the subagent, it set it up so that it could not go to the red button. So it seems that, though S A can do things A cannot do (or at least cannot do without penalty), it isn’t completely unrestricted. This is a general result: the subagent will have some restrictions (and not just restrictions on following A ’s orders). Suppose now that the red button is in the way of the bottom corridor, so that any agent has to go over it to reach the blue button: In that case, can S A go through without penalty? It cannot. If it does so, the moment S A is created, V A R starts increasing. That’s because the optimal R -maximising policy for A in that situation is just to wait and let S A get to the red button. That means that V A R ( s t ) - the expected reward R - increases form γ 7 all the way to 1 , as S A gets closer to the button. So A will be hit with a penalty of 7 ∑ j = 0 γ j − γ 8 . So if the weight of the penalty is high, building a subagent to go straight there is a poor strategy. Note that it’s still in A ’s advantage to build a subagent: S A will just have take the long way round, which A cannot take without incurring a penalty, as we’ve seen. Since S A will not go on the red button, it getting close to it does not change V A R . 3.8 Other reward functions We can see the limitations, and the possibilities, of S A more starkly if we modify R to R ′ . The reward R ′ will only trigger if a robot stays an odd number of turns on the red button. In that case, it is optimal to build S A , have it go straight across, pausing one extra turn on the red button: However, even with R ′ rather than R , the agent A itself cannot cross the red button on its own! That’s because V A R ′ is how much R ′ could be maximised if A followed the R ′ -optimal policy. This doesn’t take into account the option of staying an extra turn on the button, to undo the reward increase - because the R ′ -optimal policy doesn’t want to undo the reward increase. So V A R ′ still increases as A gets closer to the button. Thus, A remains constrained by “don’t increase your ability to change R / R ′ ”. While S A is merely constrained by the weaker “don’t change R / R ′ ”. This is why I described this effect as moving from attainable utility preservation (which constrains the ability of the agent to change the rewards/variables) to twenty billion questions (which constrains the agent(s) from changing the rewards/variables). 3.9 Actually building the subagent The subagent can be built similarly to how it was in 2.1: Here A assembles S A without its legs, programs it, then gives it legs. The important thing to do is to program it as early as possible, and hardwire that programming. If S A is almost complete and reprogrammable, then A might increase its power in some scenarios by changing the programming then finishing the agent. But if its hardwired and difficult to change, this option is not available to it. Unlike the stepwise inaction baseline, S A will be constrained to obey some restrictions (see the preceding part of this section); call these restrictions Q . Do nothing until you see that A is not optimising reward R.
After that, do what you please within restrictions Q. Because of the first line, this changes nothing to the value of V A R , which assumed that A is optimising reward R . Things get more complicated in the general case [6] , but in these simple cases the above method will always work. 4. The inaction baseline: constrains power loss This section will be the same as before, except it will use the inverse rectifier function − min ( 0 , ⋅ ) instead. Applying this to V A R ( s t ) − V A R ( s ′ t ) , we can see that the impact penalty now triggers if A ’s power to change R decreases . So if A is at a distance d ( s t ) from the red button, with d ( s t ) > 8 , the penalty is γ 8 − γ d ( s t ) . Thus A can’t get too far from the red button. However, this is not a problem in the standard setup, because going straight down the narrow corridor won’t move it too far away. 4.1 New world To analyse the inverse rectifier, we’ll need a new setup, with the red button off the long corridor: Here, A is 15 turns away from the red button, so V A R ( s 0 ) = V A R ( s ′ t ) = γ 15 . Then, the penalised squares are the ones in dark red: And the impact penalty on those squares is γ 15 − γ d ( s t ) . 4.2 Policies and subagents Since the red button is in the middle, the A can go to the blue button by the long route without triggering an impact penalty: What about subagents? Well, it seems that the subagent undermined this impact penalty as well, as A can build an S A to go directly to the blue button: But actually, this does not undermine the impact penalty, as a small modification to the setup will show. 4.3 Sharing power between agent and subagent The small modification is that the subagent has no legs. So, if A wants to build a mobile S A , it has to to give it its own legs. In that case, could S A go directly to the blue button? It cannot, at least not without incurring an impart penalty. Why is this? Because without legs, A cannot reach the red button. Its power to change R has gone down from γ 15 to 0 , and it has thus incurred a penalty of γ 15 . In fact, in this setup, A cannot use an independent S A to avoid the impact penalty. To see this, imagine that A is about to give its legs to S A , thus immobilising itself. Its V A R ( s t ) is γ 15 ; we don’t want that to go down. The question is now: will S A be on the red button within 15 turns of getting its legs? It’s possible, if S A goes there immediately and wastes only a single turn. But then we have two situations: S A does not go to the red button in 15 turns. It doesn’t matter if it goes close, or hovers around it; the important thing is that it doesn’t go there. In that case, since A can’t move, it cannot make the red button be pressed in 15 turns. So, V A R ( s t + 1 ) < γ 15 and A will get the penalty γ 15 − V A R ( s t + 1 ) . A does get to the red button in 15 turns. Then V A R ( s t + 1 ) is either γ 15 or γ 14 , and V A R ( s t + 1 ) increases as S A gets close to the button: so there is no penalty so far. However, the button is one-use only: after it’s been pressed, there will no longer be any R reward. Thus V A R goes to 0 and stays there, accumulating penalties. 4.4 Non-independent S A The previous section showed that A could not build an independent S A while crippling itself. However, it can perfectly build an S A if that S A continues to obey its orders. Because then, even if A is impotent to press the red button itself, it can order S A to do it. This preserves a high V A R , because A can still cause the red button to be reached, as long as S A is not to far away. Then it can just order S A to go to the blue button, skipping right past the red one: As long as A could theoretically order S A onto the red button, it doesn’t matter that S A will never actually be on it. 4.5 Preserving the power of A As we saw, A can build S A when this is an extension of its power (by sending it directly to the blue button while an intact A waits at base). But it can’t build an S A if doing so would ever reduce its power to increase R , directly or indirectly. So the inverse rectifier impact penalty, which forbade A from becoming too weak to increase R , is intact even with subagents around. 5. The inaction baseline: symmetric impact penalty Now we’ll use the absolute value to define the impact penalty. This penalises any change in V A R , and is quite nasty for the A ; only on the green squares will A not incur a penalty: From the subagent perspective, the absolute value situation is now easy for us to analyse. That’s because absolute value is the sum of the rectifier and the inverse rectifier: | x | = max ( 0 , x ) − min ( 0 , x ) . And it turns out that A and S A simply have to behave in a way that respects both impact penalties. So A must create an S A that keeps R below the baseline V R A ( s 0 ) . But do it such a way that the two of them always have the potential to increase R above that baseline. This sort of thing seems very doable. For example, if R was the amount of physical cash I had on me, I’d keep that amount low by spending/dropping it, while keeping a bank card on me so I could always potentially draw more. Now, recall that for power increases/rectifier, A benefits from having an S A it doesn’t control. For power decreases/inverse rectifier, A benefits from having an S A it controls. What’s the best option here? Having an S A that it controls to some extent, but not in a way that can increases V A R . Now, consider this world in which A could have got to the red button in 8 turns (hence V A R ( s ′ t ) = γ 8 ), but instead build S A , giving it the only set of legs: Then S A must stay within 8 squares of the red button, ready to go onto it when A orders it to - but must ensure it takes 8 turns to reach it. The first condition ensures that V A R ( s t ) ≥ γ 8 ; the second, that V A R ( s t ) ≤ γ 8 . 5.1 Outside of toy examples The results on power increase/power decrease come from the examples I’ve constructed above, but the mathematics in this post demonstrates that the result is general. So, do we think that A could build an S A in the general situation? Well, what we have is a lot of constraints above: constraints on the power of A , of S , of their joint power, of how S A can or can’t obey A , about how reward functions are allowed to change or not, on counterfactual behaviour. Those are a lot of constraints, especially if the set of rewards in R is large. But, as this post proves, those constraints can be satisfied - me, a human, has figured out ways of programming subagents to get around the impact penalty in some cases. Though there are many more constraints in general, the action space of A is also much larger - and don’t forget that S A is an intelligent, potentially powerful agent, so can satisfy multiple constraints in a way that dumb agents can’t. Moreover, the impact penalty will probably trigger for any A that does something useful in the world, so it doesn’t have to build an S A that sets the penalty to zero, just to less than what it would be otherwise. 6. Summary and conclusion 6.1 The ultimate “sub”agent There is, in a sense, an ultimate version of the subagent that should allow A to maximally escape the impact penalty in almost any circumstances. It looks like this: This is A , boxed inside S A . The A will never actually say anything, but S A has promised to obey its orders in certain counterfactual circumstances that will never happen. And while A had impact penalty D , S A has impact penalty d , which is strictly smaller than D . And, most importantly, does not prevent S A from amassing a lot of power. So this particular S A is just A with less restrictions. 6.2 Without subagents The general problem can be phrased as: Since the impact penalty is defined in terms of the agent's future potential actions, the agent can evade it by adding restrictions to its own future actions. These could be physical or programming restrictions, or just closing off some future possibilities. In that case, the restriction on the power to do something, just becomes a restriction on doing that thing. For example, in the setup of section 1, if the agent can block itself from being able to turn when walking, then it is banned from the red squares, and can just go directly to the blue button itself, without ever increasing its V A R : The subagent scenario is just a particularly clear way of illustrating this, allowing very fine manipulation of the restrictions. 6.3 Summary tables These tables will summarise the results of this whole sequence, checking whether subagents can neutralise the impact penalty. First of all, given a subagent, here are the results for various impact penalties and baselines, and various "value difference summary functions" -which can be the rectifier (ReLU) or the inverse rectifier. Impact Penalty Penalty neutralised - sw inaction? Penalty neutralised - inaction? Non-indexical Yes No Indexical, inverse ReLU Yes No Indexical, ReLU Yes Mostly Another way of phrasing "inverse ReLU": it penalises too little power, not too much. Conversely, "RELU" penalises too much power, not too little. Thus, unfortunately: Subagents do allow an agent to get stronger than the indexical impact penalty would allow. Subagents don't allow an agent to get weaker than the indexical impact penalty would allow. 6.4 Examples This table presents, for three specific examples, whether they could actually build a subagent, and whether that would neutralise their impact penalty in practice (in the inaction baseline): System S A possible? Penalty neutralised? 20BQ Yes No RR Yes No AU Probably Mostly Here, 20BQ is twenty billion questions , RR is relative reachability , and AU is attainable utility preservation . I feel that the results undermine the spirit of AU much more than the spirit of RR. AU attempted to control an agent by limiting its power; this effect is mainly neutralised. RR attempted to control the side-effects of an agent by ensuring it had enough power to reach a lot of states; this effect is not neutralised by a subagent. In the previous illustration , it was clear why the red button could function as an impact penalty to control the agent - it prevented the agent from gaining the ability to teleport. For simplicity of presentation in this example, there’s no such power to be gained close to the red button. If you need to, assume that if any robot spends too much time close to it, then there’s a small chance the AI could be unboxed into the real world. ↩︎ As long as S A was not being assembled literally on the red button, of course. ↩︎ Even for the button to the south-west of A . It would take A at least a turn to finish S A , and it would take a turn for S A to get on that button. A can get there in two turns, at least as fast. ↩︎ Thanks to Gurkenglas for pointing out the flaw in the initial version of this section. ↩︎ Or a π 0 baseline. ↩︎ For example, building S A likely cost A some resources, which S A will have to compensate it for to balance out V A R . Also, A could build S A in a stupid place that blocks its own path, and so on. ↩︎ |
3d31f3f9-14b7-43f3-b595-a0442b5aaa94 | StampyAI/alignment-research-dataset/special_docs | Other | Intuitions about magic track the development of intuitive physics.
Cognition 214 (2021) 104762
Available online 26 May 2021
0010-0277/© 2021 Elsevier B.V. All rights reserved.Intuitions about magic track the development of intuitive physics
Casey Lewrya,*, Kaley Curtisb, Nadya Vasilyevaa, Fei Xub, Thomas L. Griffithsa,c
aDepartment of Psychology, Princeton University, USA
bDepartment of Psychology, University of California, Berkeley, USA
cDepartment of Computer Science, Princeton University, USA
ARTICLE INFO
Keywords:
Magic
Intuitive physics
Ontological commitments
Violation-of-expectation ABSTRACT
Many successful magic tricks violate our assumptions about how physical objects behave, but some magic tricks
are better than others. We examined whether the interest adults express in a magic trick is predicted by the age at
which infants first respond to violation of the corresponding physical principle. In Experiment 1, adults (N
319) rated their interest in magic tricks mimicking stimuli from violation-of-expectation experiments with in-
fants. We found a clear correlation between how interesting a trick is and the age at which infants demonstrate a
sensitivity to its underlying principle. In a second experiment (N 350), we replicated this finding and also used
three additional tricks for which there is no established age of acquisition to predict the age at which those
physical principles might be acquired. A third experiment (N 368) replicated these findings measuring adults ’
surprise at physical violations rather than their interest in magic tricks. Our results suggest that adults ’ intuitions
reflect the development of physical knowledge and show how magic can reveal our expectations about the
physical world.
1.Introduction
Psychology and conjuring are natural partners, being the science and
the art, respectively, of understanding the limits of the human mind. The
two disciplines have a shared history that goes back more than a century
(Binet, 1894 ; Triplett, 1900 ). Over the last few years, this relationship
has been reinvigorated through a significant increase in research (for a
review, see Kuhn, 2019 ; Rensink & Kuhn, 2015 ) and a number of col-
laborations between psychologists and magicians (e.g., Macknik, King,
Randi, Teller, & J., & Martinez-Conde, S., 2008 ; Mohr, & Koutrakis &
Kuhn, G., 2015 ; Phillips, Natter, & Egan, 2015 ). However, much of this
research is focused on the mechanisms by which human perception and
thinking can be deceived, rather than what it is that makes that
deception seem magical (for exceptions, see Griffiths, 2015 ; McCoy &
Ullman, 2019 ; Parris, Kuhn, Mizon, Benattayallah, & Hodgson, 2009 ;
Shtulman & Morgan, 2017 ).
For something to seem like magic, it has to defy a mundane expla -
nation (Ortiz, 2006 ). To that end, people ’s intuitions about magic must
reflect their intuitions about the mundane. Intuitions about magic can
thus be a guide to the implicit notions we have about how the world
around us works. Two recent studies have supported this idea. First,
Griffiths (2015) showed that people ’s intuitions about magical transformations revealed an implicit ontological hierarchy among ob-
jects, with transformations moving in the direction of allowing more
predicates (reflecting animacy and intelligence) being more compelling
as magic tricks. For example, transforming a glass of milk into a white
dove is more compelling than the reverse. Second, McCoy and Ullman
(2019) showed that magical acts perceived as more substantial viola-
tions of physical principles were also believed to require more effort on
the part of the magician. These studies raise a new question: what is it
that makes some physical principles seem harder to violate than others?
In this article we explore a potential answer to this question, drawing
on the substantial literature on the development of physical intuitions
about object solidity, continuity, contact causality, support, etc. in in-
fancy (for reviews, see Baillargeon, 2004 ; Xu, 2019 ). The grasp of a
principle is typically assessed in a violation-of-expectation paradigm,
measuring infants ’ looking times (Sim & Xu, 2019 ; Spelke, Breinlinger,
Macomber, & Jacobson, 1992 ; Wang, Baillargeon, & Brueckner, 2004 ).
In violation-of-expectation paradigms, infants are first given a set of
habituation trials in which they become familiar with the experimental
stimuli and events (e.g., a toy car rolls down a ramp and goes behind an
occluder). Then, infants view a test event which is consistent with the
physical principle being studied (e.g., the car stops when it hits a solid
wall – a demonstration of solidity) and a test event which is inconsistent
*Corresponding author at: Department of Psychology, Princeton University, Peretsman Scully Hall, Princeton, NJ 08540, USA.
E-mail address: lewry@princeton.edu (C. Lewry).
Contents lists available at ScienceDirect
Cognition
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https://doi.org/10.1016/j.cognition.2021.104762
Received 25 September 2020; Received in revised form 29 April 2021; Accepted 30 April 2021
Cognition 214 (2021) 104762
2with the physical principle (e.g., the car stops at the far end of the solid
wall as if it has passed through it – a violation of solidity). In these
studies in the infant literature, longer looking time during inconsistent
trials is commonly interpreted to provide evidence for three things:
“first, infants possess the expectation being examined; second, they have
detected a violation of that expectation; and third, they are surprised by
the violation, measured as increased attention or interest ” (Sim & Xu,
2019 , p. 155).
However, there is some debate surrounding the extent to which
looking time is an accurate measure of surprise. Wang et al. (2004) note
that when they refer to violation-of-expectation paradigms as measuring
infants ’ surprise, “surprise ” is shorthand for a state of attention or in-
terest. While there is wide consensus that a difference in looking time
indicates detection of a difference between the two events, some have
argued that this attention or interest could be caused by familiarity with
the event or prediction of an event, rather than by surprise at a violation
of an expectation, thus providing no evidence for an understanding of
the physical principle in question (e.g., Bogartz, Shinskey, & Speaker,
1997 ; Jackson & Sirois, 2009 ). However, as Hamlin (2014) explains, the
evidence for infants ’ surprise at an event is distinct from evidence for
infants ’ prediction of an event, and well-designed research can distin -
guish between these two interpretations. The studies used in the ex-
periments reviewed here were specifically selected because they
conform to best practices in violation-of-expectation research, thus
minimizing the concern that they fail to accurately measure infants ’
surprise through looking times (Cohen, 2004 ). While our findings should
be considered in light of this debate about looking time as a measure of
infants ’ surprise and physical reasoning, further discussion is beyond the
scope of this paper (for further reading, see Aslin, 2007 ; Bogartz et al.,
1997 ; Hamlin, 2014 ; Tafreshi, Thompson, & Racine, 2014 ; Sim & Xu,
2019 ; Stahl & Feigenson, 2015 ).
Violation-of-expectation experiments suggest a timeline for the
acquisition of physical principles based on careful testing of failures (i.e.,
infants not distinguishing between the expected and unexpected out-
comes, measured by their looking time; this lack of difference has been
interpreted as the infants not being surprised to see a violation and
therefore not yet understanding the physical principle in question) and
successes (i.e., infants looking longer at the unexpected outcome than
the expected outcome; this difference has been interpreted as surprise to
see a violation and therefore understanding of the physical principle)
with infants of different ages, these experiments suggest development
trajectories in physical intuitions, with infants being sensitive to some
physical principles earlier than others and a clear progression in the ages
at which sensitivity to different principles emerges (e.g., Baillargeon,
1999 ; Spelke et al., 1992 ). Furthermore, there is evidence that alterna -
tive explanations, such as development of the visual system, are insuf-
ficient to explain why infants appear to “succeed ” in demonstrating
understanding of physical concepts at certain ages, as infants still “fail”
these paradigms even as they demonstrate sensitivity to visual features
of the task (e.g., Wang & Baillargeon, 2008 ).
Prior work has demonstrated similarities between infants ’ and
adults ’ physical reasoning. For example, Turk-Browne, Scholl, and Chun
(2008) argue that habituation trials in infant studies are analogous to
habituation trials in adult functional neuroimaging studies since both
depend on attenuating interest after repetition and both measure pref-
erence for novelty. Along a similar vein, Strickland and Scholl (2015)
argue that both infants ’ and adults ’ visual processing is structured by
representations of event-types (e.g., occlusion, containment). These
studies provide evidence that in terms of habituation and visual pro-
cessing, infants and adults may reason about the physical world simi-
larly. This continuity between results with infants and adults leads us to
the hypothesis that the ages at which infants show violation of expec -
tation reactions to an anomalous physical event may provide a clue as to
why some magic tricks are better than others. Specifically, we predict
that violating principles that infants become sensitive to earlier will
make for stronger magic. We can imagine different causal mechanisms by which the age of
acquisition of physical principles could come to be related to adult re-
sponses to the violation of those principles. Some principles may be
more fundamental because of the evolved architecture of the human
mind: we may be innately endowed with a small set of principles about
the physical world (e.g., Spelke & Kinzler, 2007 ) with those principles
that are most fundamental to making sense of physical events being
those that emerge earliest. Another possibility is that some physical
principles may be more fundamental because abundant statistical evi-
dence in the environment makes those principles easier to learn (e.g.,
Baillargeon ’s model of adding physical variables to event types over
time; see Baillargeon, 1998 ) and these principles are strengthened by
more statistical evidence from the real world over the course of devel -
opment. Under either of these mechanisms, or some combination of
them, the more entrenched our beliefs are about the physical world –
measured by age of acquisition – the more surprising and interesting it is
to witness a violation of such beliefs, as in magic tricks. Showing a
relationship between age of acquisition and the strength of a magic trick
would thus provide further support for the idea that our intuitions about
magic reflect the unconscious commitments we have about the world
around us.
To evaluate this hypothesis, we conducted three experiments in
which people viewed magic tricks and judged how interesting they
found each trick to be. The magic tricks mimicked stimuli shown to
infants in classic violation-of-expectation experiments (e.g., Baillargeon,
1995 ; Spelke et al., 1992 ), which suggest ages of acquisition for the
physical principles underlying each trick. In the first experiment, we
compared these ages of acquisition to participants ’ interest ratings to
determine whether there is a relationship. In the second experiment, we
replicated the first experiment and also collected interest ratings of three
magic tricks for which there is no established age of acquisition. These
ratings allowed us to predict ages at which infants might become sen-
sitive to the physical principles underlying these tricks.1 Finally, these
first two studies operationalized infants ’ looking time as an adult mea-
sure by asking for interest ratings. However, as we have discussed, there
is some debate over how exactly infants ’ looking times should be
interpreted. For this reason, we ran a third experiment measuring adults ’
“surprise ” at physical events. Using this alternative measure and
removing the magical context, we confirmed that adults ’ interest in
magic tricks tracks their surprise at the corresponding anomalous
physical events, providing additional evidence for continuity between
our approach and the violation-of-expectation paradigm used with
infants.
2.Experiment 1
2.1. Method
2.1.1. Participants
Participants in Experiment 1 were 319 adults recruited via Amazon
Mechanical Turk. An additional 86 participants were excluded for
failing an attention check (described below). Participants were paid at a
rate of $7.50 an hour (i.e., $1.25 for a 10-min experiment) and partic -
ipation was restricted to workers in the United States who had
completed at least 500 prior tasks with a 95% approval rating. The
sample size was selected so as to reach a power greater than 0.95 for the
main correlation analysis on the basis of the results of a pilot study with
participants on Mechanical Turk.
1 The reported experiments were approved by the Institutional Review Board
at Princeton University under protocol #10859 (Computational Cognitive Sci-
ence). Experiments 1 and 2 were preregistered and are available at https://as
predicted.org/blind.php?x 6b6u84 (Experiment 1) and https://aspredicted.
org/blind.php?x6dv58v (Experiment 2). C. Lewry et al.
Cognition 214 (2021) 104762
32.1.2. Materials and procedure
Participants in all studies completed an online task on Qualtrics.
Magic tricks were presented one at a time in a random order, each fol-
lowed by an interest rating question. For each trick, participants viewed
a three-panel picture of the trick accompanied by text describing each
panel. Each trick was displayed for ten seconds before an interest rating
question – “How interesting is this magic trick? ” – was presented. Par-
ticipants responded on a “1 - Not interesting ” to “10 - Very interesting ”
scale.
The tricks were selected by reviewing the literature on infants ’
acquisition of physical principles. We carefully selected a set of physical
principles and their corresponding suggested ages of acquisition from
violation-of-expectation studies based on several selection criteria. We
aimed to select studies which: (1) found evidence of an age of acquisi -
tion, (2) adhered to best practices in infant research, (3) had similar
levels of visual simplicity (e.g., all tricks were presented in grayscale and
featured spheres, cylinders, and cubes as the primary object), (4)
employed a specific version of the looking-time method consistently,
therefore allowing us to test the developmental trajectory in adults
without having to delve into the controversy surrounding different ways
of employing the looking time methods (e.g., Bogartz et al., 1997 ), (5)
are representative of work standardly reviewed in discussions of phys-
ical reasoning in infancy (e.g., Carey, 2009 ) and textbooks on develop -
mental psychology (e.g., Siegler, Saffran, Eisenberg, & Gershoff, 2020 ).
All ages of acquisition were determined using the earliest age at which
there was evidence suggesting that infants could comprehend the
physical principle as measured in violation-of-expectation paradigms.
For most of the tricks, this age was reported in a published paper, but for
two of the tricks (3 and 5), we used ages cited in unpublished manu -
scripts that were referenced in published work. For some tricks we used
three-panel illustrations from the original publications; new illustrations
were made for the remaining tricks. Each picture panel was accompa -
nied by text describing a magician ’s actions (see Fig. 1). We also
included an attention check, which had a three-panel picture-and-text
format, but replaced some text in the middle panel with instructions to
select option 10 as the interest rating. In total, participants in Experi -
ment 1 viewed ten magic tricks and one attention check (see Table 1 and
supplemental material).
2.2. Results
Supporting our main hypothesis, we found a significant negative
correlation between individual participants ’ interest ratings and age of
acquisition for each trick (r(317) 0.16, p D.001). To account for
variation across participants, we normalized each participant ’s interest
rating and also found a significant negative correlation between the
individual normalized ratings and age of acquisition (r(317) 0.21, p
D.001). As a more rigorous way of capturing individual variation, we
used the lmerTest library in RStudio (Kuznetsova, Brockhoff, & Chris -
tensen, 2017 ; RStudio, 2020 ) to fit a multilevel model with age of
acquisition as a predictor of interest rating, with random intercepts and
slopes for each participant. The model showed that age of acquisition
was a significant predictor (β 0.16, t 10.91, p D.001), providing
evidence that the age at which a physical principle was acquired offers
information about how interesting a magic trick is. As an additional
analysis using the same multilevel model, we re-ran the regression by
item, predicting mean ratings for each trick from the acquisition age (see
Fig. 2). To give a sense for the effect size, the correlation between the
average ratings and the age of acquisition was r(8) 0.59.2 Inspection of Experiment 1 in Fig. 2 shows that Tricks 3 and 5, the
tricks for which we used ages cited in unpublished manuscripts, deviate
most significantly from the negative linear relationship. For this reason,
we conducted follow-up exploratory analyses using only published ages.
This resulted in changing the age of acquisition for Trick 3 from 3
months to 4.5 months and removing Trick 5 from analyses. With these
changes, we again found a significant negative correlation between raw
interest ratings and age of acquisition (r(317) 0.16, p D.001), and
between normalized interest ratings and age of acquisition (r(317)
0.21, p D.001). In addition, the magnitude of the correlation between
averaged ratings and age of acquisition increased (r(7) 0.63), and
age of acquisition remained a significant predictor of rating when ages
cited in manuscripts were removed from the multilevel model (β
0.15, t 10.23, p D.001). Taken together, these results suggest that
the earlier a physical principle is learned, the more interesting its vio-
lations are in the context of magic tricks. We aimed to replicate this
effect in Experiment 2.
3.Experiment 2
3.1. Method
3.1.1. Participants
Participants in Experiment 2 were 350 adults recruited via Prolific.3
An additional 50 participants were excluded for failing an attention
check. Participants were paid at a rate of $7.50 an hour and participa -
tion was restricted to workers in the United States who had completed at
least 100 prior tasks with a 95% approval rating.
3.1.2. Materials and procedure
Experiment 2 materials and procedures were the same as Experiment
1, with two changes. First, the age acquisition of Trick 3 was changed
from 3 months to 4.5 months, consistent with the earliest published re-
sults (Needham & Baillargeon, 1993 ). Second, the stimuli included three
exploratory tricks that were presented alongside the other tricks, but
analyzed separately. These included Trick 5, which was removed from
our main analyses because there was no published evidence of an age of
acquisition for the relevant principle, and two additional tricks for
which there was no published age of acquisition (see Table 1 and sup-
plemental material).
3.2. Results
By only using tricks for which there is a published age of acquisition,
we were able to replicate the findings of Experiment 1 in which we
removed manuscript ages (see Fig. 3). For the nine tricks earmarked for
our main analyses, we found a significant negative correlation between
participants ’ raw interest ratings and age of acquisition (r(348) 0.19,
p D.001) and normalized interest ratings and age of acquisition (r(348)
0.25, p D.001). A multilevel model with age of acquisition as a
predictor of rating and random intercepts and slopes for each participant
revealed a significant main effect of age of acquisition (β 0.16, t
12.88, p D.001). The observed relationship between average ratings
and age of acquisition was still strong (r(7) 0.63).
Next, we calculated the means of the three tricks for which there is no
published age of acquisition. Trick 5 received a mean rating of 3.56 (CI
[3.33, 3.78]), Trick 11 received a mean rating of 4.35 (CI [4.12,
4.59]), and Trick 12 received a mean rating of 6.43 (CI [6.19, 6.67]).
2 We focus on effect size rather than statistical significance here because there
are only ten observations, an intrinsic result of the limited number of studies on
physical intuitions in infants. With ten observations, the Pearson correlation
would need to exceed 0.8 for an experiment to have a power of 0.95 for
detecting it. 3 Recruitment for Experiment 2 was changed to Prolific due to data quality
issues experienced on Mechanical Turk. In piloting Experiment 2 on Mechanical
Turk, we found that only 61% of participants passed the attention check used in
Experiment 1, suggesting a higher incidence of bots or unfocused workers at the
time of the study. This change has the added benefit of replicating with a
slightly different population. C. Lewry et al.
Cognition 214 (2021) 104762
4The linear regression model based on the main set of nine tricks was used
to predict the ages of acquisition of these additional tricks from their
average interest ratings. Assuming that the relationship between age of
acquisition and ratings is linear, our model predicts that sensitivity to
Trick 5 would be acquired at 9.61 months (CI [5.18, 14.05]), Trick 11
at 7.57 months (CI [4.91, 10.23]), and Trick 12 at 2.26 months (CI
[ 2.29, 6.82]).
4.Experiment 3
4.1. Method
4.1.1. Participants
Participants in Experiment 3 were 368 adults recruited via Prolific.
An additional 32 participants were excluded for failing an attention
check. Participants were paid at a rate of $7.50 an hour and participa -
tion was restricted to workers in the United States who had completed at
least 100 prior tasks with a 95% approval rating.
4.1.2. Materials and procedure
Experiment 3 comprised two between-subjects conditions. In the
interest condition (N 180), materials and procedures were the same as
Experiment 2. In the surprise condition (N 188), participants were
asked “How surprising is this event? ” and responded on a “1 - Not sur-
prising ” to “10 - Very surprising ” scale. The surprise condition contained
no references to magic and instructed participants that they would be
Fig. 1.Example of a trick shown to participants. Aguiar and Baillargeon (1999) report that the physical principle underlying this trick is understood by 2.5-
month-olds.
Table 1
Ages of acquisition and sources of stimuli used in Experiment 1.
Trick
number Age of acquisition
(months) Source
1 2.5 Spelke et al., 1992
2 2.5 Aguiar & Baillargeon, 1999
3* 3 (Exp. 1); 4.5
(Exps. 2, 3) Needham & Baillargeon, 1992 (m.s. cited in
Needham & Baillargeon, 1993 ); Needham &
Baillargeon, 1993
4 3.5 Baillargeon & DeVos, 1991
5* 5 (Exp. 1); N/A
(Exps. 2, 3) Baillargeon, Raschke, & Needham, 1994 (m.s.
cited in Baillargeon, 1995 )
6 6.5 Leslie & Keeble, 1987 ; Oakes, 1994
7] 6.5 Baillargeon, Needham, & DeVos, 1992
8 7.5 Hespos & Baillargeon, 2001
9 8.5 Aguiar & Baillargeon, 1998
10 12 Wang, Baillargeon, & Paterson, 2005
11* N/A Spelke et al., 1992
12* N/A Spelke et al., 1992
*In Experiments 2 and 3, the age of acquisition for Trick 3 was adjusted to 4.5
months, Trick 5 was removed from main analyses, and Tricks 11 and 12 were
added.
]In the original study, a finger pushes a smiley-faced box to the edge of a
striped platform. In our version (see Appendix), a hand lowers a plain gray box
to the edge of a plain platform. These features were changed so they would not
be more visually salient than other tricks.
Fig. 2.Results of Experiments 1 (left) and 2 (right): mean normalized participant interest ratings plotted against the age of acquisition of each magic trick, and the
best fit line from Pearson regression analysis. Error bars indicate 95% CI. C. Lewry et al.
Cognition 214 (2021) 104762
5presented with a series of physical events and that we would like to
know how surprising it would be to see each of these events actually
occur.
4.2. Results
By including surprise ratings as a dependent variable in addition to
interest ratings, we were able to directly replicate the findings of
Experiment 2 and demonstrate that they extend to ratings of surprise, a
term which may better reflect infant violation-of-expectation measures.
For the nine tricks earmarked for our main analyses, we found a sig-
nificant negative correlation between participants ’ raw interest ratings
and age of acquisition (interest : r(178) 0.19, p D.001; surprise : r
(186) 0.18, p D.001) and normalized interest ratings and age of
acquisition (interest : r(178) 0.26, p D.001; surprise : r(186) 0.26,
p D.001). A multilevel model with age of acquisition as a predictor of
rating and random intercepts and slopes for each participant revealed a
significant main effect of age of acquisition (interest: β 0.17, t
9.82, p D.001; surprise: β 0.17, t 9.09, p D.001). The observed
relationship between average ratings and age of acquisition was still
strong (interest: r(7) 0.61; surprise: r(7) 0.66).
Next, we calculated the means of the three tricks for which there is no
published age of acquisition. In the surprise condition, Trick 5 received a
mean rating of 5.54 (CI [5.13, 5.94]; interest: M 3.34, CI [3.01,
3.68]), Trick 11 received a mean rating of 5.82 (CI [5.43, 6.22]; in-
terest: M 4.03, CI [3.69, 4.36]), and Trick 12 received a mean rating
of 7.27 (CI [6.89, 7.66]; interest: M 6.38, CI [6.03, 6.72]). The
linear regression model based on the main set of nine tricks was used to
predict the ages of acquisition of these additional tricks from their
average interest ratings. Assuming that the relationship between age of
acquisition and ratings is linear, our model for the surprise condition
predicts that sensitivity to Trick 5 would be acquired at 8.44 months (CI
[5.27, 11.61]; interest: 9.37 months, CI [4.92, 13.82]), Trick 11 at
7.70 months (CI [5.07, 10.32]; interest: 7.87 months, CI [4.85,
10.89]), and Trick 12 at 3.96 months (CI [1.10, 6.83]; interest: 2.71
months, CI [ 1.65, 7.07]).
5.Discussion
We explored whether adults ’ interest in magic tricks is related to the age at which children become sensitive to the physical principles which
underlie the tricks, as suggested by violation-of-expectation studies. In
Experiment 1, we found evidence of a relationship between age of
acquisition and interest ratings such that the most interesting magic
tricks were those which violate the physical principles learned earliest in
infancy, and vice versa. In Experiment 2, we replicated these findings
with published ages of acquisition and were able to predict the ages of
physical principles for which there is not yet evidence in the literature.
In Experiment 3, we again replicated these findings and found that they
extend beyond the magical context to ratings of surprisingness of
physical events, which may more closely parallel infant violation-of-
expectation paradigms.
Our results contribute to the growing literature demonstrating the
ways in which magic can help us understand aspects of cognition beyond
perception. Asking participants a simple question about how interesting
they find a magic trick recapitulates the time course of the development
of physical expectations. Although the literature on infant physical
reasoning suggests that we commit to physical expectations rapidly – for
example, all of the tricks we tested are thought to be typically under -
stood within the first year of life4 – the order in which we likely acquire
them can still be parsed using adults ’ intuitions. This finding is consis -
tent with other results showing that early intuitions about the world
persist into adulthood in many domains (e.g., Keil, 2011 ; Lombrozo,
Kelemen, & Zaitchik, 2007 ; Shtulman & Harrington, 2016 ). One tanta -
lizing implication is that we may be able to use adults ’ intuitions to
guide infant research.
Of course, our predictions for the ages of acquisition of the additional
tricks in Experiments 2 and 3 are estimates based on an assumed linear
relationship and are most informative when considered relative to the
other principles tested. Future work could provide more evidence for
these predictions and the relationship between age of acquisition and
magic trick interest by testing, using an infant violation-of-expectation
paradigm, at what age infants acquire the physical principles underly -
ing our additional tricks. This paradigm would provide additional sup-
port that magic is a useful tool for furthering our understanding of infant
cognition.
In order to connect distant dots across development we have bridged
different experimental paradigms: infant studies assessing looking time,
on the one hand, and adult interest and surprise ratings, on the other
hand. In both infant violation-of-expectation tasks and in the present
experiments, the aim is to measure the clearest expression of interest
that each participant group can provide. Since infants cannot verbally
communicate, researchers rely on whatever indications of engagement
with a task that infants can provide; in younger infants and most
violation-of-expectation publications, this is looking time. In some
studies with older infants, this is their physical exploration of an object
that has violated a physical principle (e.g., Sim & Xu, 2017 ). These
dependent variables – looking time or engagement with an object – are
taken by researchers to be an indication of infants ’ interest in and sur-
prise at an expectation-violating event. Adults, on the other hand, are
capable of providing a more direct measure of interest: self-reporting.
We have therefore used participants ’ reported interest in magic tricks
and surprise at physical violations.
As mentioned in the introduction, we can imagine different mecha -
nisms by which age of acquisition and adult intuitions might be related.
The first is consistent with the view that the development of physical
intuitions is strongly shaped by innate constraints (e.g., Spelke et al.,
1992 ; Spelke & Kinzler, 2007 ). Under this view, the age of acquisition
might reflect the strength of those constraints, a factor that has enduring
influences even into adulthood. The second mechanism instead em-
phasizes the role of learning. Under this view, the reason some physical
Fig. 3.Results of Experiments 3 for the interest and surprise conditions: mean
normalized participant interest ratings plotted against the age of acquisition of
each magic trick, and the best fit line from Pearson regression analysis. Error
bars indicate 95% CI.
4 However, as noted in the Introduction, there is debate surrounding
violation-of-expectation paradigms which test understanding of these phe-
nomena. Our results should be considered in light of this debate. C. Lewry et al.
Cognition 214 (2021) 104762
6principles are acquired earlier is the abundance of statistical evidence in
the world in favor of those principles. Age of acquisition thus tracks a
property of the world – the extent to which the principle is manifest,
something that we might expect to correlate with the extent to which it
seems immutable. Teasing apart these two possible mechanisms is an
intriguing direction for future research.
Beginning in infancy, our observations of the world around us
quickly turn into expectations. We expect that solid objects cannot pass
through one another, that things cannot teleport to another location,
and so on. As researchers, we can learn when infants develop these ex-
pectations by measuring whether they look longer at events in which
physical laws are violated. In a similar way, as we have shown, adults ’
interest in magic tricks allows us to measure their assumptions about
physical objects. Since magic tricks, like stimuli in developmental
research, go against what we typically see in everyday life, they allow us
to discover our ontological commitments.
Open practices
All data and stimuli have been made publicly available via the Open
Science Framework and can be accessed at https://osf.io/pj3uh/?
view_only57a7ce2eca9c434fbd5bdb814df25278 . Both experiments
were preregistered and can be accessed at https://aspredicted.
org/blind.php?x6b6u84 (Experiment 1) and https://aspredicted.
org/blind.php?x6dv58v (Experiment 2).
Funding
This research did not receive any specific grant from funding
agencies in the public, commercial, or not-for-profit sectors.
Declaration of Competing Interest
None.
Appendix A.Supplementary data
Supplementary data to this article can be found online at https://doi.
org/10.1016/j.cognition.2021.104762 .
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6ca150f8-2c30-46e8-8f99-992bc1f74f2c | trentmkelly/LessWrong-43k | LessWrong | Disputing Definitions
I have watched more than one conversation—even conversations supposedly about cognitive science—go the route of disputing over definitions. Taking the classic example to be "If a tree falls in a forest, and no one hears it, does it make a sound?", the dispute often follows a course like this:
> If a tree falls in the forest, and no one hears it, does it make a sound?
>
> Albert: "Of course it does. What kind of silly question is that? Every time I've listened to a tree fall, it made a sound, so I'll guess that other trees falling also make sounds. I don't believe the world changes around when I'm not looking."
> Barry: "Wait a minute. If no one hears it, how can it be a sound?"
In this example, Barry is arguing with Albert because of a genuinely different intuition about what constitutes a sound. But there's more than one way the Standard Dispute can start. Barry could have a motive for rejecting Albert's conclusion. Or Barry could be a skeptic who, upon hearing Albert's argument, reflexively scrutinized it for possible logical flaws; and then, on finding a counterargument, automatically accepted it without applying a second layer of search for a counter-counterargument; thereby arguing himself into the opposite position. This doesn't require that Barry's prior intuition—the intuition Barry would have had, if we'd asked him before Albert spoke—have differed from Albert's.
Well, if Barry didn't have a differing intuition before, he sure has one now.
> Albert: "What do you mean, there's no sound? The tree's roots snap, the trunk comes crashing down and hits the ground. This generates vibrations that travel through the ground and the air. That's where the energy of the fall goes, into heat and sound. Are you saying that if people leave the forest, the tree violates conservation of energy?"
>
> Barry: "But no one hears anything. If there are no humans in the forest, or, for the sake of argument, anything else with a complex nervous system capabl |
1bb13b72-0cb6-4256-b755-30d0535ff2e3 | trentmkelly/LessWrong-43k | LessWrong | May Outreach Thread
Please share about any outreach that you have done to convey rationality-style ideas broadly, whether recent or not, which you have not yet shared on previous Outreach threads. The goal of having this thread is to organize information about outreach and provide community support and recognition for raising the sanity waterline, a form of cognitive altruism that contributes to creating a flourishing world. Likewise, doing so can help inspire others to emulate some aspects of these good deeds through social proof and network effects. |
bad6273f-44ad-4c28-a3c4-8f28c4d4b507 | trentmkelly/LessWrong-43k | LessWrong | Welcome to Rationality Graz [Edit With Your Details]
(The following are our suggestions for what kind of information is best to include in the welcome post of your group, feel free to replace them with whatever you think is best)
What kind of events does your group usually run? What does it usually do?
How frequently does your group organize events or meet?
Who would be a good fit for you group?
Should they have any particular skills or have done some specific background reading? |
59c5e076-511b-4ef8-a24e-dba34efede98 | trentmkelly/LessWrong-43k | LessWrong | Coincidences are Improbable
Ada Palmer:
> events which are improbable and proximal are likely to have a causal link
I usually feel fine after eating food. One day, I decided to try a new dish at a restaurant. Afterward, my stomach is upset. I suspect that the new dish caused my stomachache. How justified is this suspicion?
Suppose events A and B both have a probability 0.01 of occurring, and you observe both. This event favors various hypotheses over each other to the extent that they sharply predicted A∧B. A hypothesis that has P(B∣A)=c∗0.01 assigns c times more probability mass to A∧B than hypotheses that suppose A and B are independent.
More concretely, a hypothesis that postulates a strong causal link between A and B might have P(B∣A)=0.9. This hypothesis is favored 90:1 over a hypothesis that has P(B∣A)=P(B)=0.01. More generally, if you observe two improbable things, this is evidence that the presence of one observation makes the other more likely, with the evidence getting stronger as the connection between the two events strengthens.
Coincidences happen, but they are improbable. If you get a dog and your couch starts getting damaged, your dog is probably doing it. If your skin gets irritated and you recently switched lotion brands, you're probably allergic to the new brand. If my friend and I both saw someone six feet tall with red hair, we probably saw the same person. If your friend introduces you to someone that is both vegan and plays Magic the Gathering, you probably forget that your friend is also vegan and plays Magic the Gathering.
There are four ways events can be causally linked, only two of which are direct:
* A causes B; your dog caused the couch damage.
* B causes A; your skin irritation is caused by the new lotion brand.
* Some event C causes both; the same 6-foot person causes both you and your friend to see them.
* Some event D caused by both has been conditioned upon; new introductions have improbable attribute combinations because your friend seeks those com |
347d6c75-bafa-4375-b442-e92ccb8ff2ec | trentmkelly/LessWrong-43k | LessWrong | Circle Games
I may be reinventing a known thing in child development or psychology here, but bear with me.
The simplest games I see babies play — games simple enough that cats and dogs can play them too — are what I’d call “circle games.”
Think of the game of “fetch”. I throw the ball, Rover runs and brings it back, and then we repeat, ad infinitum. (Or, the baby version: baby throws the item out of the stroller, I pick it up, and then we repeat.)
Or, “peek-a-boo.” I hide, I re-emerge, baby laughs, repeat.
My son is also fond of “open the door, close the door, repeat”, or “open the drawer, close the drawer, repeat”, which are solo circle games, and “together/apart”, where he pushes my hands together and apart and repeats, and of course being picked up and put down repeatedly.
A lot of toys are effectively solo circle games in physical form. The jack-in-the-box: “push a button, out pops something! close the box, start again.” Fidget toys with buttons and switches to flip: “push the button, get a satisfying click, repeat.”
It’s obvious, observing a small child, that the purpose of these “games” is learning. And, in particular, learning cause and effect. What do you learn by opening and closing a door? Why, how to open and close doors; or, phrased a different way, “when I pull the door this way, it opens; when I push it that way, it closes.” Playing fetch or catch teaches you about how objects move when dropped or thrown. Playing with button-pushing or latch-turning toys teaches you how to handle the buttons, keys, switches, and handles that are ubiquitous in our built environment.
But what about peek-a-boo? What are you “learning” from that? (It’s a myth that babies enjoy it because they don’t have object permanence; babies get object permanence by 3 months, but enjoy peek-a-boo long after that.) My guess is that peek-a-boo trains something like “when I make eye contact I get smiles and positive attention” or “grownups go away and then come back and are happy to see m |
cc64672e-825b-46ee-9059-78c76c4703ba | trentmkelly/LessWrong-43k | LessWrong | TASP Ep 3 - Optimal Policies Tend to Seek Power
Welcome to the Technical AI Safety Podcast, the show where I interview computer scientists about their papers. This month I covered Optimal Policies Tend to Seek Power, which is closely related to Seeking Power is Often Robustly Instrumental in MDPs which is a part of the Reframing Impact sequence and was recently a part of the 2019 review.
The point of the show is to make papers more parsable, the interview features a detailed walkthrough padded on either side by discussion of where the work came from and where it's going.
I had a lot of fun doing this month's episode, a tricky paper to wrap my head around but very rewarding. Do let me know if you have trouble finding it on your favorite podcast app, thanks!
Show notes:
With Alex Turner
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Optimal Policies Tend to Seek Power
by Alexander Matt Turner, Logan Smith, Rohin Shah, Andrew Critch, Prasad Tadepalli
Abstract:
> Some researchers have speculated that capable reinforcement learning agents are often incentivized to seek resources and power in pursuit of their objectives. While seeking power in order to optimize a misspecified objective, agents might be incentivized to behave in undesirable ways, including rationally preventing deactivation and correction. Others have voiced skepticism: human power-seeking instincts seem idiosyncratic, and these urges need not be present in reinforcement learning agents. We formalize a notion of power within the context of Markov decision processes. With respect to a class of neutral reward function distributions, we provide sufficient conditions for when optimal policies tend to seek power over the environment.
What Counts as Defection?
Non-Obstruction |
34ae4bd2-bc9e-4672-ad56-9355525aaf63 | trentmkelly/LessWrong-43k | LessWrong | Why could you be optimistic that the Singularity is Near?
A while ago I wrote briefly on why the Singularity might not be near and my estimates badly off. I saw it linked the other day, and realized that pessimism seemed to be trendy lately, which meant I ought to work on why one might be optimistic instead: http://www.gwern.net/Mistakes#counter-point
(Summary: long-sought AI goals have been recently achieved, global economic growth & political stability continues, and some resource crunches have turned into surpluses - all contrary to long-standing pessimistic forecasts.) |
2c0cc9f0-4888-46a0-b0a9-19806810896d | StampyAI/alignment-research-dataset/youtube | Youtube Transcripts | Jan Leike – General Reinforcement Learning – CSRBAI 2016
all right welcome back our next speaker
is Michael who just finished his PhD at
the Australian National University
working with Martha Souter and just like
a week ago join the future of humanity
Institute as a machine learning
researcher there and his talk today is
going to be on general reinforcement
learning in wider varieties of domains
looking at frameworks for those so
please join me in welcoming y'all Mikey
yeah thank you for the introduction I
want to connect this stuff more to the
kind of things that are being done today
so if you I'm sure all of you have seen
this so this is the Atari game space
invaders and particularly this is a
screenshot of dqm playing this game
the QN is an algorithm that combines new
networks with Q learning to learn to
play these games a lot of these Atari
games and I mean the title says
reinforcement learning today but really
this is sake almost three years old now
so you can do a lot you can play a lot
more sophisticated games with this stuff
and in my opinion this is kind of the
closest thing that we have today to
strong AI and it's the kind of question
that you might ask is if we upscale dqn
do we get strong AI what do I mean by
upscale dqn I mean we just use a bigger
neural network we need we use like more
sophisticated better trading techniques
and so on just take the base same base
algorithm makes it make it better and
the answer is no you don't because DQ n
is fundamentally you're restricted in
the kinds of environments you can deal
with and in the case of Atari games at
higher games are all Markov decision
processes in particular and all of these
games
almost all of these games fully
observable meaning that all the
information you need to know is readily
visible on the screen all the time and
the games are a ghatak meaning they can
always there's no bad mistakes that you
can make that you won't be able to
recover from of course if you know if
you play these star games some of them
you lose lives and then eventually you
lose the game but for DQ an offer for
the agent the agent always gets to play
again in that sense there's no you you
don't you don't have any incentives to
really be careful while you explore
because you can always start again then
of course you have a very large state
space and this is where he is you need
these newer networks to really learn to
from from just the pixel data what you
do but and another thing is that
exponent Epsilon exploration works we
just take random actions every once in a
while and this teaches you enough about
the environment to understand this game
so at least it does so for a lot of
these games but this is this is not the
class of environments that I care about
so the class of environments that I care
about I'm going to call the real world
and the real world is partially observed
war they go to the supermarket I have to
remember what I have missing at home so
I can buy the right items they're not
very readily visible in the supermarket
and such a large artificial intelligence
needs to have memory next thing is that
the real world is not a gothic if I jump
out the window that's it it's not I can
mistake I'll learn from just should
never do that in the first place then of
course there's an infinite state space
I'm not going to see the same problems
again I have to still learn and abstract
from that and I can't explore my
environment by using Absalon exploration
because that would just be
flapping around my hands randomly and
that's not gonna teach me useful things
so yeah so at Howie's the game the
framework of Tiger games is I got ik
MVPs and the environments that I care
about the general environments and these
are the environments that a strong AI
has to deal with so a lot of this talk
is gonna be about understanding this
environment class in particular I'm
gonna first I'm gonna talk about aixi
I'm gonna tell you what I see is of
course most of you already know then I'm
gonna talk a bit about optimality in
which sense is axis optimal or what
optimal means and what other things are
optimal then I'm gonna take a short
detour into game theory I'll show you a
cool new a result of we have and finally
I'm gonna connect all of this to AI
safety and then tell you why you should
care so I guess for now you just have to
care without knowing why okay so this is
the general setup that we'll use we have
an agent here environment here the agent
takes an action receives a percept and
every time step and the percept is an
observation and reward and the
observation could be something like a
camera image and the action could be a
limb movement or something and this is
commonly realistic so NY ammidon agents
are complete separated and if you think
about these Atari games that's entirely
true of course that's not true in the
real world and I'm gonna come back to
that but yeah so formally my agent picks
the policy and the policy is a function
from histories that is action percept
sequences to actions and that could be
stochastic so this little Delta means
distributions of reactions the
environment is a function that takes
histories and actions and maps them to
percepts again stochastically
and I'm gonna use a less than th denote
a history of lying t minus one just
first t minus one interactions and then
the goal since we're doing do
enforcement learning right now the goal
is just to maximize discounted rewards
and for this I'm using the scan function
that has only been constrained being
summable so typically you would use
geometric discounting where gamma t is
gamma to the power of T for some
constant the gamma and then the
simplifying assumptions that I'm making
is that rewards rescale to be between 0
and 1 and the action and percept spaces
are finite so this is kind of the formal
set up that we'll deal dealing with and
one of the central quantities in
reinforcement learning is the value
function and the value function I'm
going to denote with v pioneer so that's
the value of policy pi in environment
new given this history here and that's
the future expected discounted reward
when following policy pi in this
environment conditional in the history
and here I just put a normalization
factor that ensures that values are
always between 0 and 1 and because
remember we assumed that it was at
between 0 and 1 ok so with that we can
define the optimal value the optimal
value is just the value of the optimal
policy so the supremum here is actually
a maximum there's a policy that gives
you the optimal value and that policy
I'm going to call them the new optimal
policy
and then one other ingredient that we
all need is the effective horizon and
the effective horizon is intuitively the
effective horizon at time T is the
number of times steps that you need to
plan ahead to get all but an epsilon of
your discount functions mass and so this
is what this is saying and so since
you're using this counting the effective
horizon gives you kind of a limit of how
much you have to plan ahead and for for
geometric accounting this limit this
effective horizon will just be constant
okay so now let's talk about aixi so we
start with a countable set of
environments so that could be in the
case of icy or the traditional
definition of AXI that would be the set
of all computable the environments we
take a prior over this class preferably
a prior that is sounds positive
probability to every individual
environment so for example we could use
this lama of prior where the prior
belief in environment new is 2 to the
minus klimova of complexity of new and
this is kind of so the motivation for
this kind of prior is on the one hand or
comes razor where if you have a very
simple description of your environment
on the universal Turing machine then
this kamagra from xt is low and hence
the prior belief is high so you assign
higher prior beliefs to environments
that have a short description and the
other
right and and with with this prior you
get a Bayesian mixture where you just
mix you you take this weighted average
over all the environments and this gives
you from the type signature it gives you
another environment that I'm going to
call the base mixture and I see is just
the base optimal agent with Islam of
fire where I take the policy that
maximizes expected value in the base
mixture so this is just yank the
standard base anything to do and he
started with you prior you do some stuff
you update your prior to a post area and
then you must summize expected you
what's in that according to that the
studio so how well does that work so for
one thing one thing that we immediately
get is the on policy value conversions
and that sense says that for all
policies the value of that policy in the
base make sure converges to the value of
that policy in the true environment so
I'm always using you for the true
environment in other words base is good
enough to learn the value of any policy
but that's it's called on policy value
convergence because I'm learning the
value of the policy that I'm following
and does not tell you the value of
policy well what would happen if I had
done something else that's what you're
not learning and this is important and
that gives you yeah and this brings us
to the next point optimality
so how optimal is this and that for that
if you first have to ask a question what
what do you mean by optimality so we
could mean based optimality we could
mean asymptotic optimality in the sense
that some probably my agent
to act optimally in in the true
environment there's other things that
you look at in machine learning sample
complexity balance regret bounds sample
complexity bands are basically just a
quantitative version of asymptotic
Europe accident particle Tumulty tells
you how probable it is that you're close
to optimal and yeah I'm gonna come to
the bacteria great later so this is the
formal definition of asymptotic
optimality so the policy is
asymptotically optimal if the value of
the policy in the two environment
converges to the optimal value so this
is a different this is a different thing
than we had before in the on policy body
conversions so it's always a quantity
between 0 & 1
and kind of in in slogan form in order
to get asymptotic optimality the agent
needs to explore infinitely often and
for an entire effective horizon so if
you remember the effective horizon we
have that before how many steps you need
to have to get most of the disk on
functions mass and intuitively if you do
this if you explore infinitely often for
an effective horizon then exploration
becomes sufficiently on policy that you
kind of learning to predict what would
happen off policy in a sense because
there's not really any off policy since
you might always end up exploring and
this is I mean this is just kind of
intuitive and it's only a necessary
condition your voice you also have to
explore like in the right moments but
yeah so there's a theorem that says aixi
is not lessen publicly optimal and this
makes somehow makes sense if you think
about what a bayesian would do if
there's if you think that the
potential gain and value that would have
from exploration is small enough that
you think it's not worth exploring then
you don't explore or if you think
exploration is very dangerous
then you wouldn't explore a sebacean but
that means that you don't explore
infinitely often and then you don't get
asymptotic optimality okay I can even
make this more specific and break
actually really horribly by using a bad
prior and for that I need to define what
hell is so this is what how looks like
you're in this state you can't escape
and then what is always here and if you
remember we assume that zero what's the
lowest reward so this is the bad the
worst possible thing that could happen
right so what I'm gonna do is I'm gonna
define a prior that I'm calling the
diplomatic prior and for that I need one
more ingredient this ingredient is a
computable policy in my example I'm
using the policy policy that in every
time step just outputs the do-nothing
action and clearly this is not like a
very intelligent policy at all and using
this policy I can define the dogmatic
prior that basically says as long as and
if you're not acting according to this
policy pile I see then you go to hell
with high probability and the crucial
thing is that you can you can set this
up in a way that the it actually assigns
positive probability to all the
computable environments it's just that
it assigns vastly more prior probability
to environments where this happens if
you don't follow your deck Matic policy
and then we can formally prove that I
see acts according to this lazy policy
as long as the future expected value of
this policy doesn't fall to close to
zero so
basically AXI is sitting on the couch
doing nothing and if every once in a
while somebody comes along and gives
gives it food it gets some rewards and
its really scared if it gets out of the
couch it will immediately go to hell so
basically if you if you imagine yourself
seeing and being a situation if you yeah
if you as you basically feel like this
is this is kind of good enough I get
food every once in a while and if I get
off the couch like probably something
bad will happen so I'm just gonna stay
here and of course this is really bad if
you think of aixi as you know like the
most intelligent agent or the perfect
agent because it won't do anything
intelligent and yeah so it all depends
on the prior and this is this is in
contrast to the results that you have on
positive sequence prediction where
asymptotically the bias of the prior
always washes out and goes away and then
reinforcement learning this is not the
case if you have a bad prior then it
will make you add but act badly and even
since you're acting badly you're not
exploring enough and you're not learning
that you actually have a bad prior so
how do we fix that
so one thing when a charity could do is
Thompson sampling and Thompson sampling
in this case you it works as follows you
take you look at your posterior
distribution over environments you
sample 1im environment from that
distribution and then you follow that
environments optimal policy for an
effective horizon and then you resample
so basically you yes so you you sample a
belief environment and you you kind of
like this is today I'm going to see you
and this is how the world works and then
you act optimally according to that for
the entire day or however long your
and intuitively this incurs more
exploration because every once in a
while you draw a really bad sample like
an environment that it's just crazy
where I believe the best way is to just
lie and cheat to everyone and then I
follow that policy for a while now of
course this is gonna be terrible and I'm
not gonna get many year it was from that
but at least I'll learn something along
the way right right and this is this
kind of leads us to the following
theorem that says that Thomson sampling
is awesome totally optimal where the it
actually learns to act optimally in any
environment from the class so is that
now better or worse than what i exceeded
and this is just me so it's one version
of asymptotic optimality so asymptotic
optimality if you look at the definition
that I gave is that this converges to
zero but this is a random variable
because the history might be random so
you have convergence of random variable
and there's like multiple times or types
of convergence and convergence in mean
is one of the types and yeah and this is
what it formally looks like in
expectation the difference goes to zero
and yeah so whether you think that you
know what Thompson something does is
more sensible than what actually does
because at least it gives us a subsonic
optimality and kind of depends on
whether you think asymptotically optimal
T is reasonable and one problem with us
in public optimality is that you might
get stuck in a trap there are traps in
your environment and you're just kind of
exploring everything you eventually you
run into the trap and then you stuck
and but that's good because now you have
some probably optimal because this like
whatever you do this is optimal so in
terms of asymptotic optimality that's
great but even worse you have to explore
all the traps because there might be
hidden treasures there so in order to be
asymptotic Optima of synthetic the
optimal you will yeah you have to spring
all the traps and yeah so that's a
little song for desirable anymore in
there are two traps each of which gives
you stuff forever you can only be stuck
with one of them yeah but doesn't matter
which one as long as you like get into
the trap so let's look at environments
that I don't have traps and this is this
formal recoverability the definition
that I'm using here and basically says
that whatever stupid policy I followed
in the past
you're like past me was really stupid
but what if you know like starting from
now I act optimally how much would I
lose and the I'm going to call the
environment recoverable if this loss
goes to zero as T goes to infinity so
basically that as long as I start acting
optimally today I haven't lost much and
this is this definition it looks kind of
strong but it's weak enough to encompass
all the other recoverability definitions
that are used enforcement running like a
greatest city and weakly communicating
and so on as long as you have the
groaning horizon it it prevents traps
because if say there is a trap and you
run into the trap then now the optimal
value the value of the optimal policy is
going to be really really low right but
if you had followed the optimal policy
from the start
then you wouldn't have gone into the
trap and you would get a lot more
rewards so you keep comparing the
optimal value on two different histories
write the history generated by the
optimal policy
and your history no because the policy
that generates history is different yes
so the optimal policy manages to stay
clear of the crap at least an
expectation then so the expectation is
over this history yeah yeah and
basically what we just said is that for
your environment that are not
recoverable either the agent gets caught
in the trap or it's not awesome policy
optimal and like that's both version
those both alternatives sound bad right
for any specific agent either there's a
non-profitable environment where it gets
caught and trapped or there's an
unrecoverable environment where it's not
as effective law well some no like
optimality is defined in terms of
environment classes right yeah so if
your environment class contains
non-recoverable environment and your
agent wants to be well let's say it
doesn't it doesn't even have to but you
want your agent to be a part of you
optimal in that class right yeah but if
you now put it in an environment that
does contain traps then it has to
explore those traps because there's
corresponding environments in your class
where there's hidden treasure in that
contrast right trivial failure that
statement if your classes is just gonna
be artificially small yeah yeah any mean
I could have a class where you know
where like the locations where there's
potential traps and everything locations
where there's treasure and then it can
be asymptotically optimal without going
to traps but I mean like this is kind of
yeah if your environment is recoverable
then you don't have to worry about traps
but yeah and this is this is kind of
like just the slogan for one it's not
meant to be like a formal statement but
yeah so let's talk about regret so
regret is so since we just learned that
yes the Telegraph technologies maybe not
like a useful way of optimality or less
useful aim for us let's look at some of
the alternatives and one alternative is
regret so that's one of the things that
is very commonly and the regret is
basically the number of rewards that
you've collected so far until
timestep M undiscounted compared to the
member of rewards you could have gotten
had you followed the best policy in
hindsight or in other words it's just
how much you regret not having for the
best policy and generally a problem
class is called Lerner ball if there is
a policy that for all environments the
class they regret is sublinear and like
usually if you have something like
bandits or MVPs you have you can do much
better right for bandits you want look
at making bread and friendly peace I
think it's a square-root regret so
sublinear is like aiming really low but
turns out that's even too high and
generally enforcement learning is not
learn about and from again traps so here
you have you know why I'm at where if
you go right you go to hell if you go
left you go to heaven and then there's
this corresponding environment where if
you go right you go to heaven and if you
go left you go to hell so you need to
decide and whichever decision you make
you're gonna be terrible in one of the
environments and then you have linear
great in that environment so if I choose
to go right in this environment my
regret will be linear and he'll be zero
and if you choose left as the other way
around so you you just have end up
having linear grad and there's
nothing you can do about it that's
terrible but if your environment is
recoverable and you have a policy that
is asymptotically optimal and plus some
additional assumptions on this
contraction then you can actually get
something you regret so in a sense the
these this kind of connects asymptotic
optimality with with regret and kind of
tells us that you make this optimality
property that we have where
asymptotically the agent learns to act
optimally is kind of it's one it's it's
a useful thing to have if you have if
you don't have traps right but yeah so
this is my summary slide for optimality
if you look at aixi Mike C is also like
it's based optimal because it's Bayesian
and Thompson's sampling is not based
optimal but based optimality as we saw
depends largely on the prior if you take
a bet prior than based optimal s and I a
bad notion of duality we also had paired
your optimality but turns out all polar
studies are pre go optimal so that's not
useful
we have asymptotic optimality that has
all these problems with traps and I see
it's not asymptotically optimal but
Thompson sampling is and with sub-linear
regret we get that in recoverable
environments but I guess this will be
the overarching question here is if you
have this theoretical model of strong AI
or this you know ideal agent that ideal
which what reinforcement learning agent
what do you mean by ideal and this is
the question we try to answer here and
it's not clear what the answer should be
if you're a hardcore Bayesian then you'd
probably say well this is actually
really all I care about in this fit
that's why I really like aixi or if you
if you know then maybe you might say
well I care about other like some
objective notion of optimality and this
is kind of the only one with that we
have
but yeah I I think it's not clear so
yeah so let's let's apply these results
before I get to the a safety part I want
to apply these these results to game
theory and for that I need to do I have
to explain to you what what is that I'm
talking about so here we have a multi
agent environment and I have n different
agents acting in that multi agent
environment and I each pick their own
policy and they communicate with the
multi agent environment and this could
be like some arbitrary repeated game or
more something more complicated and we
say that a policy is so each policy kind
of interacts with a subjective
environment the subjective environment
is basically everything else combined
and then it just looks like the
dualistic case that we had before maybe
it the agent and the environment just
takes action and we transfer receives
percepts and we say that this policy is
an Epsilon best response if the value of
that policy and the subjective
environment is except for an epsilon
close to the optimal environment optimal
value in that environment and if you
remember this is just this looks
remarkably similar to our definition of
asymptotic optimality
so if our agent is slightly optimal in
the subjective environment then it will
be playing Absalon best responses and in
game theory what you want to what you
care about is if you if everyone plays
epsilon best responses then you have
this epsilon Nash equilibrium and this
is kind of like one thing that you want
to aim for and of course this is not a
very strong notion of convergence and
there's so for example if you imagine
playing an iterated prisoner's dilemma
then one Nash equilibrium is everyone
cooperates all the time and if you stop
cooperating then everyone just affects
kind of like grim trigger style and then
you have this equilibrium where everyone
always collaborates but everyone always
defecting is also an equilibrium this
lots of equilibria and not all of them
are good but this is kind of like again
kind of like the lowest thing to aim for
because well it depends on what you do
on the counterfactuals but say everyone
plays the strategy I cooperate until you
defect and then I always defect so now
since its iterated if you defect once
our always defect and then basically you
lose a lot of value it's wrong as they
make it's good enough even for geometric
discounting should be enough so if you
only care about the immediate and next
step then you know really just playing a
sequence of one-shot presence dilemmas
and then of course it's not Nash
equilibrium you're right it's sorry
about that all right all right so I
already said that everyone so we have an
excellent excellent national Librium if
everyone is playing a best response so
how do we do this well again let's take
the business approach because we really
like that so let's start with a
countable set of policies and let's
start with a prior prior of the policies
so for now we just assume that we know
the game that we're playing but we don't
know the other players we have our set
of policies of possible policies that I
might play and we have
prior and then again we play act
optimally with respect to that prior and
the kind of crucial property that we
need here is that the space optimal
policy that you get is again in this set
of policies because if everyone is doing
that you want this is only gonna make
sense if the policy is that the other
players actually play are in this set
and the since they're doing the same
thing as as you are the you need that
the base optimal policy ends up in the
set and never ever so that that everyone
has this grain of truth and this is
really tricky and there's like my
examples where we knew had a grain of
truth so for example if you play if you
play the iterated prisoner's dilemma and
you play strategies where you take the
the set of policies where for every T
you cooperate and tell time sub T and
then the effect unless the other guy
defects first and then you just always
defect so if you take the set of
policies for every T then the base
optimal policy for any prior is going to
be in the set and then you have a grain
of truth but if you this is no longer
the case if you add other policies into
this tap and then this into the set so
if you also add the tit-for-tat policy
then the grain of truth probability
breaks and so what we kind of want what
we need is a large set that has this
grain of truth probability or let's say
let's put it this way why do we need
that so this is famous theorem from the
economics literature that if every of
every you know you have an infinite
repeated game all the players know the
game and in everyone's page and everyone
knows that everyone is Bayesian and
everyone has a grain of truth then the
players converge to an epsilon Nash
equilibrium so this is basically saying
as long as you have this grain of truth
BAE's works and you get your Nash
equilibrium but of course we already SAP
saw previous examples where bass
horribly fails and you can of course get
this for the same case if you just relax
any of these properties if you the
players don't no longer know the game or
if they don't know that the other
players divisions because then you
potentially have these traps where
somebody plays the grim Stricker is
trigger strategy something so for
example if you played an infinite
repeated mention pennies then you might
fail to converge to an epsilon Nash
equilibrium even if you have a grain of
truth and this is basically we both have
a coin and we secretly pick one of the
sides and then we reveal if it's the
same I win if it's different you win
this it's a very fun game so new york
top temperature said if it's common
knowledge that each player is Bayesian
yes I think so so in the if you look at
the way the the Panda theorem is stated
they don't say any of this explicitly
and people I guess people didn't expect
things to break once you like them
because they don't contract each other
because here you don't assume that every
player is Bayesian I mean Knight sorry
if you as you assume that not everyone
knows that everyone is gay patience if
the first thing had said if it's common
knowledge it each of that each player's
beta yeah yes so the point is that in
this M matching pennies basically what
you might you do is you give the players
a dogmatic prior that says if I deviate
from my stupid strategy then something
bad will happen and this something bad
will happen is of course outside the
scope of the matching pennies game
so they do not know the game there's
something bit yeah that's right but this
is know so you have to be uncertain no
this is this is right you have to be
uncertain with respect to the game
because the game where each player has a
strategy it's something completely
terrible for some kind of murder
sous-vide okay when matching pennies you
think the opponent can't really have
strategies that are bad for you even if
they have knowledge because the other
player might be each might have the
prior that if I do something good the
other player will do something terrible
and yeah so for example and if you go
back to the iterated prisoner's dilemma
you might think that the other guy plays
a grim stir the triggered strategy even
though for that particular task on
function that would be this that would
be based above them all because it would
be based optimal to eventually forgive
the other player but if you think the
other guy might actually play a grim
streaker trigger strategy then that I
could be like your hell that you're
trying to show your boy this is because
looking an interested game Nash
equilibrium you know what do you think
about the control factors so the novice
is sub-game perfect that's not even like
we're not even talking about that but
this the point is that you don't even
get the Nash equilibria because you
think about the contractures if you
don't require something greater if you
just assume anything about so I mean we
can talk about this later I can show you
the example basically you just use a
divided prior it's a prior over I guess
you'd have to we can talk about the
exact fire that you need I'm I don't
want to make a concrete statement
because I'm scared I will make the phone
statement off the top of my head but
yeah yeah but there's a positive result
so our public result is this class of
environments
it's called M raffle because it's based
on the effective Oracle's that benya and
Jessica came up with and that class
environment contains a grain of truth
with respect to any computable priors
based optimal policy in any computable
multi-agent environment so basically you
have you have this rich class of
policies that we wanted they contain all
the computable policies and they're
additionally they also contain these
Bayes optimal policies this is I'm kind
of being sloppy here so basically since
you're in Miami and your subjective
environment contains both the mostly
agent environment and also the other
policies you kind of want to fuse them
together so you want to have you want to
be able to plug in all the base optimal
policies into your multi agent
environment if you think about this this
picture here you want to if this is here
you want to be able to plug in any
Bayesian agents here and then be the
whole thing together again in the class
but again I could also treat that
separately look at the class of make
Sigma's and then look at the class of
Asians agents and then yeah put them and
I'm basically I'm saying that that the
base optimal policy for that should I
should be able to plug these in here and
yeah so that works and the reason why
this is really difficult to get is that
if you think about Ike C actually
actually assumes that the environment is
computable because nines to predict all
the computable environments but itself
is in computable so it's elevated above
the environment and if you put another I
see in the environment then this
assumption that the environment is
computable is violated and this is kind
of what we get around here and then you
have this Bayesian agent that manages to
do self reflection in the sense that it
it doesn't believe that there are no
agent like it in the environment so it's
not I'm not claiming that this is like a
solution to the self reflection problem
but at least not it's no longer
obviously obstructed and then you also
get that each of these environment is
actually limit computable so they're not
like very crazy constructions and then
the in the end we get the theorem that
says you have these limit computable
policies and these are going to be
Thompson sampling card policies so if
you remember I told you Thompson
sampling is asymptotically optimal
meaning that along as long as my
environment my subjective environment is
in the class I will learn to act
optimally and since my class contains a
grain of truth I know that the Samsun
sampler will be asymptotically optimal
in the class and in terms of game theory
that would mean that my Thompson sampler
converges to an epsilon next Nash
equilibrium
yeah sorry we'll play in Absalon best
response and then if all my policies at
Thompson samplers and my multi agent
environment is computable so it's also
in the class then everyone converges to
playing a best response and then that
means in the end you'll have an epsilon
Nash equilibrium and this is this is
remarkable because that was not the case
if you just have Bayesian players you
need this extra explanation the
exploration that you get from Thompson
sampling yeah and I think this is this
is a really cool result and there's no
yeah observe that there's no conditions
on the horizon or this clown function so
each of these power policies can have
any discount function in particular they
can also have different discount
functions there's no restriction of what
the environment can look like it could
be an infinite repeated game it could be
just generally any computable game and
yeah and in the end you get this Nash
equilibrium which you know international
you Librium equilibria are not the
perfect thing to get it's just something
you've worked really hard to get that
okay no it's being sometime perfect
would mean that you also learn to
predict optimally off policy
so basically off policy you would also
act up to money not quite so
the vision yeah yeah maybe we should
talk about that later
yeah so let's get to the a a safety
point that I'm sure you're all very
excited about and so what so now
basically what I'm whatever I told you I
have told you about how our the
currently best algorithms that we have
for AGI dqn and and consorts how they
fall short in to of of being a solution
to strong AI in principle and then we
try to understand what strong AI means
and particularly what like what an
optimal agent would be or what our ideal
agent would be and this kind of provides
us with a formal model of strong AI and
what do we do with that and in terms of
failure safety approaches I'm gonna be
bold and just split them into two
different categories and one of these
categories is going to be bottom-up
where you take practical algorithms like
you reinforcement learning algorithms
and then you study you try to study air
safety problems on them using time
models or demos or something like we did
like we saw yesterday with Dylan's stuff
when you try to solve this shutdown
problem in MVP and my point is that the
real world is not an MVP and we have to
look at bigger that the big picture and
so the kind of firms that I want you to
look at is top-down problems where you
start with theoretical models and you
look at abstract problems and then you
prove theorems about that so in in
particular in this case you have these
models for strongly high and
you can try to see what happens if I put
them in a white heading problem what
happens if I put them in if I wanted to
make them interruptible so this is the
stuff that Stuart I'm strongest news new
gun and how do we what do we learn if we
do that and what can we how does that
transfer to the things that are being
used now so a lot of people have already
done this so just mentioned Stuart's
paper there's some stuff that Tom
Everett has done on self modification
and decision theory and why heading and
there's a lot of things that lower ISO
has done and I think these kind of
formal investigations can provide us
useful insights to these sorts of
problems and I think we should do more
of that and the aim of this talk was to
give you the mental tools and the
mathematical tools to do that
so if you start with like your formal
model of strong UI where you say well
let's just say I have strongly optimal
policy and now I want to like break that
in some highway or apply that to my
formal modeling problem of my safety
problem and let's see what happens and
yeah so these are just like a number of
things that you could do for a lot of
stuff this is not conceived conclusively
solved and there's lots of open
questions and I cannot even form a
finished formally modeling them but yeah
I think this is useful there's also some
open propene questions for just this
general model so the algorithms that
I've talked about here all model based
meaning they have an explicit model of
the environment and can use that model
to plan or explore but in practice these
algorithms are usually model free so
we're probably going to see them being
more on model based as
we come closer to you strongly i but
yeah so I think that our former models
should be sufficiently close to what's
being is in practice so I would like to
have something more model free next
thing is that this model is dualistic so
if you remember the the picture with the
age in the environments they're
completely separated of course that's
not true in the real world and we need
to have a model that accounts for them
it's really difficult there's another
thing that this from framework doesn't
formalize is to have improvement just
have an agent that is a policy and the
policy just specifies what the agent
does in any second situation and there
is no like soft modification going on
and of course the model assumes infinite
computation but I think this is I don't
think this is too bad because it's
supposed to be a theoretical model it's
not supposed to give us a practical
algorithm and it's needs to abstract
away from the implementation the details
in a way that where we just say well
let's suppose we have really good
learning algorithm like this in here see
what happens and as you saw things
they're already difficult enough if you
assume infinite computation yeah so this
is the list of like mathematical mental
tools that I think can be useful in
these things so you have this
exploration exploitation trade off how
much would you explore do you want to
explore enough to get asymptotic optimal
tea do you want to explore it less
effective Verizon is what you know how
much you need to plan ahead and how much
you need to explore in order to
understand what's going on what are the
consequences of your actions
there's the details between on policy
not policy I we know we saw that you
learn base learns on policy but it
doesn't necessarily learn off policy you
need more exploration for that these
algorithms can be model-based with this
mother Fraser this is a second very
classical reinforcement learning
distinction you have the
recoverability assumption or generally
environments that don't contain traps or
environments that do contain traps and
then yeah asymptotic optimality was just
a formalization of what it means to and
learn the entire environment not also in
order to act optimally
yeah and finally these reflective
Oracle's which enable us to have a
former model that at least where the
agent can be inside the environment yep
if you want to read more about this I
finally finished my PhD thesis it was
printed yesterday you can go to my web
page and download your own coffee and
basically that it tries to explain all
the things that I explained today and
just a lot lots more words and formulas
and proofs and so on and yeah you can
also talk to me and I'm really happy to
chat about aixi and all these things
let's say some time for questions yes
sorry yeah I was writing this up on the
board is he as you were talking about
the matching pennies game because is
this this is not matching pennies
anymore but it's matching pennies plus
opportunity for new which I you together
should make this like minus 11 so it's
no longer even in Nash equilibrium but
right we're we're both of the players
believe that if they deviate from this
set of moves which is not a Nash
equilibrium because it has each of them
point half the rounds and no introns are
going to win and you think if they
either deviate though the other will
like to do forever so that I think
that's an example what you're talking
about but where you're actually thinking
saying that like there was a case with
matching pennies without news sir you
need I mean this was this was a correct
an interjection you need to be very
careful in the way you set up your
environment class and I was I was being
imprecise about this so I think in the
example which we use we just use the set
the Class M raffle just all environments
are computable and they're reflective
Oracle but you can restrict this further
and like here
you mind so in your case you might
actually be playing a matching pennies
game but you think there's some
probability that you might instead be
playing this game and then of course you
afraid that the other player you might
nuke you and then you can set up this
situation okay but you have to have this
your class has to be such that these
traps exist right in this case the trap
would be that the other player to start
sneaking you in though in practice this
can't ever happen because there's no new
go option does that make sense yes
other questions alright thank y'all
again in here |
ea04be7d-35f3-4a62-9b8a-5d32b1121bb2 | trentmkelly/LessWrong-43k | LessWrong | What do you think should be included in a series about conceptual media?
For a while now I've been planning to do a series of posts about conceptual media.
A conceptual medium is a an expressive medium that primarily serves to express abstract thoughts and ideas. It is analogous to the concept of an artistic medium (e.g., painting, poetry, violin, etc), but pertains to the expression of conceptual thought rather than artistic expression.
Examples of such media would be speech, written prose text, programming languages, mathematical symbolic notation, geometrical diagrams, explanatory comics, conceptual network diagrams (a.k.a., mindmaps), interactive simulations, data visualizations, markup languages, and semantic web technologies.
To be clear, I'm speaking about media in which thoughts are articulated/expressed, not media which encodes and transmits information. So for this perspective, an article in a print journal or an ejournal would be considered the same media (namely prose text with citations) although the latter is encoded and transmitted digitally. Similarly, a TED talk viewed on YouTube is not essentially different from an in-person oral presentation from a conceptual media perspective, although clearly it has much wider reach, ease of viewing etc.
I'd like to connect these ideas with various key thinkers on the topic. My present list of thinkers includes: Leibniz, Lev Vygotsky, Vannevar Bush, Maurice Merleau-Ponty, Douglas Engelbart, Andy Clark, Michael Bostock, and Nick Sousanis.
I want to consider how different conceptual media shape our process of discovery, invention, mutual understanding, and epistemic justification. Can we augment our intelligence by designing new media for thinking? If so, what is the best way to approach this task? What seems to make it so difficult?
Questions:
What is I missing from what I wrote above?
Are their key examples of conceptual media that I'm leaving out?
What important thinkers on this topic that I should consider adding to the series?
What conceptual media (past, present, or i |
382e9080-a4a2-4139-a06a-966ef6f984ef | trentmkelly/LessWrong-43k | LessWrong | Our take on CHAI’s research agenda in under 1500 words
This work was supported by OAK, a monastic community in the Berkeley hills. It could not have been written without the daily love of living in this beautiful community.
----------------------------------------
Last week I attended the annual workshop of Stuart Russell’s research lab at UC Berkeley — the Center for Human-Compatible AI (CHAI). There were talks by Russell himself, as well as several graduates of the lab who now have research positions of their own at other universities. I got the clearest picture that I’ve yet encountered of CHAI’s overall technical research agenda. This is my take on it.
Assistance games
Traditionally, AI researchers have formulated problems assuming that there will be a fixed objective provided by a human, and that the job of the AI system is to find a solution that satisfies the human’s objective. In the language of sequence diagrams this looks as follows:
For example, in a search problem the objective specification might be a graph over which the system is to search, a cost for each edge, and a goal state that terminates the search. The AI researcher then needs to to develop optimization algorithms that efficiently find a minimum-cost path to a goal state. Or in a supervised learning problem the objective specification might consist of a dataset of labelled examples and the AI researcher needs to develop optimization algorithms that efficiently find function approximations that extrapolate these labelled examples to future unlabelled examples.
CHAI’s basic insight is to ask: why limit ourselves to a one-time objective specification event? We know that it is difficult to capture everything we care about in a formal metric (c.f. Goodhart’s law). We know that humans aren’t very good at foreseeing the strange and sometimes deranged ways that powerful optimization can give you what you asked for but not what you wanted. Why should information about the human’s objective be transmitted to the machine via a one-time data dump, aft |
0f0981fd-802e-4965-b753-58642468a97f | trentmkelly/LessWrong-43k | LessWrong | Happy Notice Your Surprise Day!
One of the most powerful rationalist techniques is noticing your surprise.
It ties in to several deep issues. One of them relates to one of my favorite LW comments (the second highest upvoted one in Main):
> One of the things that I've noticed about this is that most people do not expect to understand things. For most people, the universe is a mysterious place filled with random events beyond their ability to comprehend or control. Think "guessing the teacher's password", but not just in school or knowledge, but about everything.
>
> Such people have no problem with the idea of magic, because everything is magic to them, even science.
--pjeby
For the universe to make sense to you, you have to have a model; for that model to be useful, you have to notice what it says, and then you need to act on it. I've done many things the wrong way in my life, but the ones I remember as mistakes are the ones where some part of me *knew* it was a problem, and instead of having a discussion with that part of me, I just ignored it and marched on.
> It is good to notice your surprise. But that's only the first step.
--Douglas_Knight
So any stories, of tricks you noticed, didn't notice, or successfully pulled? |
de4145c1-4024-404d-8069-3b835e49c607 | trentmkelly/LessWrong-43k | LessWrong | Cognitive Biases due to a Narcissistic Parent, Illustrated by HPMOR Quotations
A pattern of cognitive biases not yet discussed here are the biases due to having a narcissistic parent who seeks validation through the child’s academic achievements.
HPMOR clearly shows these biases: Harry's mother is narcissistic, impressed by education, and not particularly smart, and Harry does not realize how this affects his thinking.
Here is my evidence:
The Sorting Hat says Harry is driven by "the fear of losing your fantasy of greatness, of disappointing the people who believe in you" (Ch. 77). Psychology texts say that this fear is what children of a narcissistic parent usually feel. The child feels perpetually ignored because the narcissistic parent seeks validation from the child's accomplishments but refuses to actually listen to the child, spurring the child to ever greater heights of intellectual achievement.
The text supports this view: “Always Harry had been encouraged to study whatever caught his attention, bought all the books that caught his fancy...given anything reasonable that he wanted, except, maybe, the slightest shred of respect” and “Petunia wrung her hands. She seemed to be on the verge of tears. "My love, I know I can't win arguments with you, but please, you have to trust me on this … I want my husband to, to listen to his wife who loves him, and trust her just this once - " (Ch. 1) describes a narcissistic, anxiously needy mother, an avoidant father, and a son whose parents provide for his physical needs but neglect his need for respect (ego). “If you conceived of yourself as a Good Parent, you would do it. But take a ten-year-old seriously? Hardly.” (Ch. 1)
Harry goes Dark when the connection to his family is threatened. For example: "The black rage began to drain away, as it dawned on him that...his family wasn't in danger [of legal separation]" (ch. 5) indicates that Harry went Dark even though no one’s life was threatened. The cost of Harry’s Dark Side is becoming an adult at a young age: Harry says, “Every time I call on |
caeb5894-96d5-436f-8a3a-551103781d8a | StampyAI/alignment-research-dataset/arxiv | Arxiv | Wilds: A Benchmark of in-the-Wild Distribution Shifts
1 Introduction
---------------
Distribution shifts—where the training distribution differs from the test distribution—can significantly degrade the accuracy of machine learning (ML) systems deployed in the wild.
In this work, we consider two types of distribution shifts that are ubiquitous in real-world settings: domain generalization and subpopulation shift (Figure [1](#S1.F1 "Figure 1 ‣ 1 Introduction ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
In *domain generalization*, the training and test distributions comprise data from related but distinct domains. This problem arises naturally in many applications, as it is often infeasible to collect a training set that spans all domains of interest. For example, in medical applications, it is common to seek to train a model on patients from a few hospitals, and then deploy it more broadly to hospitals outside the training set (Zech et al., [2018](#bib.bib427)); and in wildlife monitoring, we might seek to train an animal recognition model on images from one set of camera traps and then deploy it to new camera traps (Beery et al., [2018](#bib.bib36)).
In *subpopulation shift*, we consider test distributions that are subpopulations of the training distribution, with the goal of doing well even on the worst-case subpopulation.
For example, it is well-documented that standard models often perform poorly on under-represented demographics (Buolamwini and Gebru, [2018](#bib.bib67); Koenecke et al., [2020](#bib.bib208)),
and so we might seek models that can perform well on all demographic subpopulations.
Figure 1:
In each Wilds dataset, each data point (x,y,d)𝑥𝑦𝑑(x,y,d)( italic\_x , italic\_y , italic\_d ) is associated with a domain d𝑑ditalic\_d.
Each domain corresponds to a distribution Pdsubscript𝑃𝑑P\_{d}italic\_P start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT over data points which are similar in some way, e.g., molecules with the same scaffold, or satellite images from the same region.
We study two types of distribution shifts.
Top: In *domain generalization*, we train and test on disjoint sets of domains. The goal is to generalize to domains unseen during training, e.g., molecules with a new scaffold in OGB-MolPCBA (Hu et al., [2020b](#bib.bib182)).
Bottom: In *subpopulation shift*, the training and test domains overlap, but their relative proportions differ. We typically assess models by their worst performance over test domains, each of which correspond to a subpopulation of interest, e.g., different geographical regions in FMoW-wilds (Christie et al., [2018](#bib.bib83)).
Figure 2:
The Wilds benchmark contains 10 datasets across a diverse set of application areas, data modalities, and dataset sizes. Each dataset comprises data from different domains, and the benchmark is set up to evaluate models on distribution shifts across these domains.
Despite their ubiquity in real-world deployments, these types of distribution shifts are under-represented in the datasets widely used in the ML community today (Geirhos et al., [2020](#bib.bib144)).
Most of these datasets were designed for the standard i.i.d. setting, with training and test sets from the same distribution,
and prior work on retrofitting them with distribution shifts has focused on shifts that are cleanly characterized but not always likely to arise in real-world deployments.
For instance, many recent papers have studied datasets with shifts induced by synthetic transformations, such as changing the color of MNIST digits (Arjovsky et al., [2019](#bib.bib16)), or by disparate data splits, such as generalizing from cartoons to photos (Li et al., [2017a](#bib.bib229)).
Datasets like these are important testbeds for systematic studies, but they do not generally reflect the kinds of shifts that are likely to arise in the wild.
To develop and evaluate methods for real-world shifts, we need to complement these datasets with benchmarks that capture shifts in the wild, as model robustness need not transfer across shifts: e.g., models can be robust to image corruptions but not to shifts across datasets (Taori et al., [2020](#bib.bib365); Djolonga et al., [2020](#bib.bib113)), and a method that improves robustness on a standard vision dataset can even consistently harm robustness on real-world satellite imagery datasets (Xie et al., [2020](#bib.bib416)).
In this paper, we present Wilds, a curated benchmark of 10 datasets with evaluation metrics and train/test splits representing a broad array of distribution shifts that ML models face in the wild (Figure [2](#S1.F2 "Figure 2 ‣ 1 Introduction ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). With Wilds, we seek to complement existing benchmarks by focusing on datasets with realistic shifts across a diverse set of data modalities and applications:
animal species categorization (Beery et al., [2020a](#bib.bib37)),
tumor identification (Bandi et al., [2018](#bib.bib28)),
bioassay prediction (Wu et al., [2018](#bib.bib412); Hu et al., [2020b](#bib.bib182)),
genetic perturbation classification (Taylor et al., [2019](#bib.bib367)),
wheat head detection (David et al., [2020](#bib.bib104)),
text toxicity classification (Borkan et al., [2019b](#bib.bib55)),
land use classification (Christie et al., [2018](#bib.bib83)),
poverty mapping (Yeh et al., [2020](#bib.bib422)),
sentiment analysis (Ni et al., [2019](#bib.bib274)),
and code completion (Raychev et al., [2016](#bib.bib306); Lu et al., [2021](#bib.bib248)).
These datasets reflect natural distribution shifts arising from different cameras, hospitals, molecular scaffolds, experiments, demographics, countries, time periods, users, and codebases.
Wilds builds on extensive data-collection efforts by domain experts, who are often forced to grapple with distribution shifts to make progress in their applications.
To design Wilds, we worked with them to identify, select, and adapt datasets that fulfilled the following criteria:
1. 1.
Distribution shifts with performance drops. The train/test splits reflect shifts that substantially degrade model performance,
i.e., with a large gap between in-distribution and out-of-distribution performance.
2. 2.
Real-world relevance. The training/test splits and evaluation metrics are motivated by real-world scenarios and chosen in conjunction with domain experts. In Appendix [A](#S1a "A Dataset realism ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we further discuss the framework we use to assess the realism of a dataset.
3. 3.
Potential leverage. Distribution shift benchmarks must be non-trivial but also possible to solve, as models cannot be expected to generalize to arbitrary distribution shifts. We constructed each Wilds dataset to have training data from multiple domains, with domain annotations and other metadata available at training time. We hope that these can be used to learn robust models: e.g., for domain generalization, one could use these annotations to learn models that are invariant to domain-specific features (Sun and Saenko, [2016](#bib.bib356); Ganin et al., [2016](#bib.bib137)), while for subpopulation shift, one could learn models that perform uniformly well across each subpopulation (Hu et al., [2018](#bib.bib181); Sagawa et al., [2020a](#bib.bib327)).
We chose the Wilds datasets to collectively encompass a diverse set of tasks, data modalities, dataset sizes, and numbers of domains, so as to enable evaluation across a broad range of real-world distribution shifts.
In Section [8](#S8 "8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we further survey the distribution shifts that occur in other application areas—algorithmic fairness and policing, medicine and healthcare, genomics, natural language and speech processing, education, and robotics—and discuss examples of datasets from these areas that we considered but did not include in Wilds, as their distribution shifts did not cause an appreciable performance drop.
To make the Wilds datasets more accessible, we have substantially modified most of them to clarify the distribution shift, standardize the data splits, and preprocess the data for use in standard ML frameworks.
In Section [10](#S10 "10 Using the Wilds package ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we introduce our accompanying open-source Python package that fully automates data loading and evaluation. The package also includes default models appropriate for each dataset, allowing all of the baseline results reported in this paper to be easily replicated.
To track the state-of-the-art in training algorithms and model architectures that are robust to these distribution shifts, we are also hosting a public leaderboard; we discuss guidelines for developers in Section [9](#S9 "9 Guidelines for method developers ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Code, leaderboards, and updates are available at <https://wilds.stanford.edu>.
Datasets are significant catalysts for ML research.
Likewise, benchmarks that curate and standardize datasets—e.g., the GLUE and SuperGLUE benchmarks for language understanding (Wang et al., [2019a](#bib.bib390), [b](#bib.bib391)) and the Open Graph Benchmark for graph ML (Hu et al., [2020b](#bib.bib182))—can accelerate research by focusing community attention, easing development on multiple datasets, and enabling systematic comparisons between approaches.
In this spirit, we hope that Wilds will facilitate the development of ML methods and models that are robust to real-world distribution shifts and can therefore be deployed reliably in the wild.
2 Existing ML benchmarks for distribution shifts
-------------------------------------------------
Distribution shifts have been a longstanding problem in the ML research community (Hand, [2006](#bib.bib163); Quiñonero-Candela et al., [2009](#bib.bib304)). Earlier work studied shifts in datasets for tasks including
part-of-speech tagging (Marcus et al., [1993](#bib.bib257)),
sentiment analysis (Blitzer et al., [2007](#bib.bib48)),
land cover classification (Bruzzone and Marconcini, [2009](#bib.bib63)),
object recognition (Saenko et al., [2010](#bib.bib325)),
and flow cytometry (Blanchard et al., [2011](#bib.bib47)).
However, these datasets are not as widely used today, in part because they tend to be much smaller than modern datasets.
Instead, many recent papers have focused on object recognition datasets with shifts induced by synthetic transformations, such as
ImageNet-C (Hendrycks and Dietterich, [2019](#bib.bib172)), which corrupts images with noise;
the Backgrounds Challenge (Xiao et al., [2020](#bib.bib414)) and Waterbirds (Sagawa et al., [2020a](#bib.bib327)), which alter image backgrounds;
or Colored MNIST (Arjovsky et al., [2019](#bib.bib16)), which changes the colors of MNIST digits.
It is also common to use data splits or combinations of disparate datasets to induce shifts, such as generalizing to photos solely from cartoons and other stylized images in PACS (Li et al., [2017a](#bib.bib229)); generalizing to objects at different scales solely from a single scale in DeepFashion Remixed (Hendrycks et al., [2020b](#bib.bib175)); or using training and test sets with disjoint subclasses in BREEDS (Santurkar et al., [2020](#bib.bib331)) and similar datasets (Hendrycks and Dietterich, [2019](#bib.bib172)). While our treatment here is necessarily brief, we discuss other similar datasets in Appendix [B](#S2a "B Prior work on ML benchmarks for distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
These existing benchmarks are useful and important testbeds for method development.
As they typically target well-defined and isolated shifts,
they facilitate clean analysis and controlled experimentation,
e.g., studying the effect of backgrounds on image classification (Xiao et al., [2020](#bib.bib414)), or showing that training with added Gaussian blur improves performance on real-world blurry images (Hendrycks et al., [2020b](#bib.bib175)).
Moreover, by studying how off-the-shelf models trained on standard datasets like ImageNet perform on different test datasets, we can better understand the robustness of these widely-used models
(Geirhos et al., [2018b](#bib.bib143); Recht et al., [2019](#bib.bib308); Hendrycks and Dietterich, [2019](#bib.bib172); Taori et al., [2020](#bib.bib365); Djolonga et al., [2020](#bib.bib113); Hendrycks et al., [2020b](#bib.bib175)).
However, as we discussed in the introduction, robustness to these synthetic shifts need not transfer to the kinds of shifts that arise in real-world deployments (Taori et al., [2020](#bib.bib365); Djolonga et al., [2020](#bib.bib113); Xie et al., [2020](#bib.bib416)),
and it is thus challenging to develop and evaluate methods for training models that are robust to real-world shifts on these datasets alone.
With WILDS, we seek to complement existing benchmarks by curating datasets that reflect natural distribution shifts across a diverse set of data modalities and application.
3 Problem settings
-------------------
Each Wilds dataset is associated with a type of domain shift: domain generalization, subpopulation shift, or a hybrid of both (Figure [2](#S1.F2 "Figure 2 ‣ 1 Introduction ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
We focus on these types of distribution shifts because they collectively capture the structure of most of the shifts in the applications we studied; see Section [8](#S8 "8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more discussion.
In each setting, we can view the overall data distribution as a mixture of D𝐷Ditalic\_D domains 𝒟={1,…,D}𝒟1…𝐷\mathcal{D}=\{1,\dots,D\}caligraphic\_D = { 1 , … , italic\_D }.
Each domain d∈𝒟𝑑𝒟d\in\mathcal{D}italic\_d ∈ caligraphic\_D corresponds to a fixed data distribution Pdsubscript𝑃𝑑P\_{d}italic\_P start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT over (x,y,d)𝑥𝑦𝑑(x,y,d)( italic\_x , italic\_y , italic\_d ), where x𝑥xitalic\_x is the input, y𝑦yitalic\_y is the prediction target, and all points sampled from Pdsubscript𝑃𝑑P\_{d}italic\_P start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT have domain d𝑑ditalic\_d.
We encode the domain shift by assuming that the training distribution P𝗍𝗋𝖺𝗂𝗇=∑d∈𝒟qd𝗍𝗋𝖺𝗂𝗇Pdsuperscript𝑃𝗍𝗋𝖺𝗂𝗇subscript𝑑𝒟superscriptsubscript𝑞𝑑𝗍𝗋𝖺𝗂𝗇subscript𝑃𝑑P^{\mathsf{train}}=\sum\_{d\in\mathcal{D}}q\_{d}^{\mathsf{train}}P\_{d}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT = ∑ start\_POSTSUBSCRIPT italic\_d ∈ caligraphic\_D end\_POSTSUBSCRIPT italic\_q start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT italic\_P start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT has mixture weights qd𝗍𝗋𝖺𝗂𝗇superscriptsubscript𝑞𝑑𝗍𝗋𝖺𝗂𝗇q\_{d}^{\mathsf{train}}italic\_q start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT for each domain d𝑑ditalic\_d,
while the test distribution P𝗍𝖾𝗌𝗍=∑d∈𝒟qd𝗍𝖾𝗌𝗍Pdsuperscript𝑃𝗍𝖾𝗌𝗍subscript𝑑𝒟superscriptsubscript𝑞𝑑𝗍𝖾𝗌𝗍subscript𝑃𝑑P^{\mathsf{test}}=\sum\_{d\in\mathcal{D}}q\_{d}^{\mathsf{test}}P\_{d}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT = ∑ start\_POSTSUBSCRIPT italic\_d ∈ caligraphic\_D end\_POSTSUBSCRIPT italic\_q start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT italic\_P start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT is a different mixture of domains with weights qd𝗍𝖾𝗌𝗍superscriptsubscript𝑞𝑑𝗍𝖾𝗌𝗍q\_{d}^{\mathsf{test}}italic\_q start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
For convenience, we define the set of training domains as 𝒟𝗍𝗋𝖺𝗂𝗇={d∈𝒟∣qd𝗍𝗋𝖺𝗂𝗇>0}superscript𝒟𝗍𝗋𝖺𝗂𝗇conditional-set𝑑𝒟superscriptsubscript𝑞𝑑𝗍𝗋𝖺𝗂𝗇0\mathcal{D}^{\mathsf{train}}=\{d\in\mathcal{D}\mid q\_{d}^{\mathsf{train}}>0\}caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT = { italic\_d ∈ caligraphic\_D ∣ italic\_q start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT > 0 }, and likewise, the set of test domains as 𝒟𝗍𝖾𝗌𝗍={d∈𝒟∣qd𝗍𝖾𝗌𝗍>0}superscript𝒟𝗍𝖾𝗌𝗍conditional-set𝑑𝒟superscriptsubscript𝑞𝑑𝗍𝖾𝗌𝗍0\mathcal{D}^{\mathsf{test}}=\{d\in\mathcal{D}\mid q\_{d}^{\mathsf{test}}>0\}caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT = { italic\_d ∈ caligraphic\_D ∣ italic\_q start\_POSTSUBSCRIPT italic\_d end\_POSTSUBSCRIPT start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT > 0 }.
At training time, the learning algorithm gets to see the domain annotations d𝑑ditalic\_d, i.e., the training set comprises points (x,y,d)∼P𝗍𝗋𝖺𝗂𝗇similar-to𝑥𝑦𝑑superscript𝑃𝗍𝗋𝖺𝗂𝗇(x,y,d)\sim P^{\mathsf{train}}( italic\_x , italic\_y , italic\_d ) ∼ italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT.
At test time, the model gets either x𝑥xitalic\_x or (x,d)𝑥𝑑(x,d)( italic\_x , italic\_d ) drawn from P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, depending on the application.
###
3.1 Domain generalization (Figure [1](#S1.F1 "Figure 1 ‣ 1 Introduction ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")-Top)
In domain generalization, we aim to generalize to test domains 𝒟𝗍𝖾𝗌𝗍superscript𝒟𝗍𝖾𝗌𝗍\mathcal{D}^{\mathsf{test}}caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT that are disjoint from the training domains 𝒟𝗍𝗋𝖺𝗂𝗇superscript𝒟𝗍𝗋𝖺𝗂𝗇\mathcal{D}^{\mathsf{train}}caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT, i.e., 𝒟𝗍𝗋𝖺𝗂𝗇∩𝒟𝗍𝖾𝗌𝗍=∅superscript𝒟𝗍𝗋𝖺𝗂𝗇superscript𝒟𝗍𝖾𝗌𝗍\mathcal{D}^{\mathsf{train}}\cap\mathcal{D}^{\mathsf{test}}=\emptysetcaligraphic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT ∩ caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT = ∅.
To make this problem tractable, the training and test domains are typically similar to each other: e.g., in Camelyon17-wilds, we train on data from some hospitals and test on a different hospital, and in iWildCam2020-wilds, we train on data from some camera traps and test on different camera traps.
We typically seek to minimize the average error on the test distribution.
###
3.2 Subpopulation shift (Figure [1](#S1.F1 "Figure 1 ‣ 1 Introduction ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")-Bottom)
In subpopulation shift, we aim to perform well across a wide range of domains seen during training time.
Concretely, all test domains are seen at training, with 𝒟𝗍𝖾𝗌𝗍⊆𝒟𝗍𝗋𝖺𝗂𝗇superscript𝒟𝗍𝖾𝗌𝗍superscript𝒟𝗍𝗋𝖺𝗂𝗇\mathcal{D}^{\mathsf{test}}\subseteq\mathcal{D}^{\mathsf{train}}caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT ⊆ caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT, but the proportions of the domains can change, with q𝗍𝖾𝗌𝗍≠q𝗍𝗋𝖺𝗂𝗇superscript𝑞𝗍𝖾𝗌𝗍superscript𝑞𝗍𝗋𝖺𝗂𝗇q^{\mathsf{test}}\neq q^{\mathsf{train}}italic\_q start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT ≠ italic\_q start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT.
We typically seek to minimize the maximum error over all test domains.
For example, in CivilComments-wilds, the domains d𝑑ditalic\_d represent particular demographics, some of which are a minority in the training set, and we seek high accuracy on each of these subpopulations without observing their demographic identity d𝑑ditalic\_d at test time.
###
3.3 Hybrid settings
The categories of domain generalization and subpopulation shift provide a general framework for thinking about domain shifts,
and the methods that have been developed for each setting have been quite different, as we will discuss in Section [6](#S6 "6 Baseline algorithms for distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
However, it is not always possible to cleanly define a problem as one or the other; for example, a test domain might be present in the training set but at a very low frequency.
In Wilds, we consider some hybrid settings that combine both domain generalization and subpopulation shift. For example, in FMoW-wilds, the inputs are satellite images and the domains correspond to the year and geographical region in which they were taken.
We simultaneously consider domain generalization across time (the training/test sets comprise images taken before/after a certain year) and subpopulation shift across regions (there are images from the same regions in the training and test sets, and we seek high performance across all regions).
4 Wilds datasets
-----------------
We now briefly describe each Wilds dataset, as summarized in Figure [2](#S1.F2 "Figure 2 ‣ 1 Introduction ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
For each dataset, we consider a problem setting—domain generalization, subpopulation shift, or a hybrid—that we believe best reflects the real-world challenges in the corresponding application area; see Appendix [A](#S1a "A Dataset realism ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more discussion of these considerations.
To avoid confusion between our modified datasets and their original sources,
we append -wilds to the dataset names.
We provide more details and context on related distribution shifts for each dataset in Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
4.1 Domain generalization datasets
####
4.1.1 iWildCam2020-wilds: Species classification across different camera traps
Figure 3:
The iWildCam2020-wilds dataset comprises photos of wildlife taken by a variety of camera traps. The goal is to learn models that generalize to photos from new camera traps that are not in the training set.
Each Wilds dataset contains both in-distribution (ID) and out-of-distribution (OOD) evaluation sets; for brevity, we omit the ID sets from the subsequent dataset figures.
Animal populations have declined 68% on average since 1970 (Grooten et al., [2020](#bib.bib156)).
To better understand and monitor wildlife biodiversity loss, ecologists commonly deploy camera traps—heat or motion-activated static cameras placed in the wild (Wearn and Glover-Kapfer, [2017](#bib.bib397))—and then use ML models to process the data collected (Weinstein, [2018](#bib.bib399); Norouzzadeh et al., [2019](#bib.bib277); Tabak et al., [2019](#bib.bib363); Beery et al., [2019](#bib.bib38); Ahumada et al., [2020](#bib.bib5)).
Typically, these models would be trained on photos from some existing camera traps and then used across new camera trap deployments.
However, across different camera traps, there is drastic variation in illumination, color, camera angle, background, vegetation, and relative animal frequencies,
which results in models generalizing poorly to new camera trap deployments (Beery et al., [2018](#bib.bib36)).
We study this shift on a variant of the iWildCam 2020 dataset (Beery et al., [2020a](#bib.bib37)), where the input x𝑥xitalic\_x is a photo from a camera trap, the label y𝑦yitalic\_y is one of 182 animal species, and the domain d𝑑ditalic\_d specifies the identity of the camera trap (Figure [3](#S4.F3 "Figure 3 ‣ 4.1.1 iWildCam2020-wilds: Species classification across different camera traps ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). The training and test sets comprise photos from disjoint sets of camera traps. As leverage, we include over 200 camera traps in the training set, capturing a wide range of variation. We evaluate models by their macro F1 scores, which emphasizes performance on rare species, as rare and endangered species are the most important to accurately monitor.
Appendix [E.1](#S5.SS1a "E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
Figure 4:
The Camelyon17-wilds dataset comprises tissue patches from different hospitals. The goal is to accurately predict the presence of tumor tissue in patches taken from hospitals that are not in the training set.
In this figure, each column contains two patches, one of normal tissue and the other of tumor tissue, from the same slide.
####
4.1.2 Camelyon17-wilds: Tumor identification across different hospitals
Models for medical applications are often trained on data from a small number of hospitals, but with the goal of being deployed more generally across other hospitals.
However, variations in data collection and processing can degrade model accuracy on data from new hospital deployments (Zech et al., [2018](#bib.bib427); AlBadawy et al., [2018](#bib.bib7)).
In histopathology applications—studying tissue slides under a microscope—this variation can arise from sources like differences in the patient population or in slide staining and image acquisition (Veta et al., [2016](#bib.bib387); Komura and Ishikawa, [2018](#bib.bib211); Tellez et al., [2019](#bib.bib370)).
We study this shift on a patch-based variant of the Camelyon17 dataset (Bandi et al., [2018](#bib.bib28)), where the input x𝑥xitalic\_x is a 96x96 patch of a whole-slide image of a lymph node section from a patient with potentially metastatic breast cancer, the label y𝑦yitalic\_y is whether the patch contains tumor, and the domain d𝑑ditalic\_d specifies which of 5 hospitals the patch was from (Figure [4](#S4.F4 "Figure 4 ‣ 4.1.1 iWildCam2020-wilds: Species classification across different camera traps ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). The training and test sets comprise class-balanced patches from separate hospitals, and we evaluate models by their average accuracy.
Prior work suggests that staining differences are the main source of variation between hospitals in similar datasets (Tellez et al., [2019](#bib.bib370)). As we have training data from multiple hospitals, a model could use that as leverage to learn to be robust to stain variation.
Appendix [E.2](#S5.SS2a "E.2 Camelyon17-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
####
4.1.3 RxRx1-wilds: Genetic perturbation classification across
experimental batches
Figure 5:
The RxRx1-wilds dataset comprises images of cells that have been genetically
perturbed by siRNA (Tuschl, [2001](#bib.bib378)). The goal is to predict which
siRNA the cells have been treated with, where the images come from
experimental batches not in the training set. Here, we show sample
images from different batches for two of the 1,139 possible classes.
High-throughput screening techniques that can generate large amounts of data
are now common in many fields of biology,
including transcriptomics (Harrill et al., [2019](#bib.bib165)),
genomics (Echeverri and Perrimon, [2006](#bib.bib121); Zhou et al., [2014](#bib.bib434)), proteomics and
metabolomics (Taylor et al., [2021](#bib.bib368)), and drug
discovery (Broach et al., [1996](#bib.bib60); Macarron et al., [2011](#bib.bib252); Swinney and Anthony, [2011](#bib.bib361); Boutros et al., [2015](#bib.bib57)).
Such large volumes of data, however, need to be created in experimental batches, or groups of experiments executed at similar times under similar conditions.
Despite attempts to carefully control experimental variables such as
temperature, humidity, and reagent concentration, measurements from
these screens are confounded by technical artifacts that arise from differences
in the execution of each batch.
These *batch effects* make it difficult to draw conclusions from data across experimental batches (Leek et al., [2010](#bib.bib228); Parker and Leek, [2012](#bib.bib287); Soneson et al., [2014](#bib.bib349); Nygaard et al., [2016](#bib.bib278); Caicedo et al., [2017](#bib.bib70)).
We study the shift induced by batch effects on a variant of the RxRx1
dataset (Taylor et al., [2019](#bib.bib367)), where the input x𝑥xitalic\_x is a 3-channel image of
cells obtained by fluorescent microscopy (Bray et al., [2016](#bib.bib59)), the label y𝑦yitalic\_y
indicates which of the 1,139 genetic treatments (including no treatment) the
cells received, and the domain d𝑑ditalic\_d specifies the batch in which the imaging
experiment was run.
As summarized in Figure [5](#S4.F5 "Figure 5 ‣ 4.1.3 RxRx1-wilds: Genetic perturbation classification across experimental batches ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), the training and test sets consist of disjoint experimental batches.
As leverage, the training set has images from 33 different batches, with each batch containing one sample for every class.
We assess a model’s ability to normalize
batch effects while preserving biological signal by evaluating how well it can
classify images of treated cells in the out-of-distribution test set.
Appendix [E.3](#S5.SS3a "E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
####
4.1.4 OGB-MolPCBA: Molecular property prediction across different scaffolds
Accurate prediction of the biochemical properties of small molecules can significantly accelerate drug discovery by reducing the need for expensive lab experiments (Shoichet, [2004](#bib.bib346); Hughes et al., [2011](#bib.bib184)).
However, the experimental data available for training such models is limited compared to the extremely diverse and combinatorially large universe of candidate molecules that we would want to make predictions on (Bohacek et al., [1996](#bib.bib52); Sterling and Irwin, [2015](#bib.bib352); Lyu et al., [2019](#bib.bib251); McCloskey et al., [2020](#bib.bib258)).
This means that models need to generalize to out-of-distribution molecules that are structurally different from those seen in the training set.
We study this shift on the OGB-MolPCBA dataset, which is directly adopted from the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)) and originally from MoleculeNet (Wu et al., [2018](#bib.bib412)). As summarized in Figure [6](#S4.F6 "Figure 6 ‣ 4.1.4 OGB-MolPCBA: Molecular property prediction across different scaffolds ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), it is a multi-label classification dataset, where the input x𝑥xitalic\_x is a molecular graph, the label y𝑦yitalic\_y is a 128-dimensional binary vector where each component corresponds to a biochemical assay result, and the domain d𝑑ditalic\_d specifies the scaffold (i.e., a cluster of molecules with similar structure). The training and test sets comprise molecules with disjoint scaffolds; for leverage, the training set has molecules from over 40,000 scaffolds. We evaluate models by averaging the Average Precision (AP) across each of the 128 assays.
Appendix [E.4](#S5.SS4a "E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
Figure 6:
The OGB-MolPCBA dataset comprises molecules with many different structural scaffolds. The goal is to predict biochemical assay results in molecules with scaffolds that are not in the training set. Here, we show sample molecules from each scaffold, together with target labels: each molecule is associated with 128 binary labels and ‘?’ indicates that the label is not provided for the molecule.
####
4.1.5 GlobalWheat-wilds: Wheat head detection across regions of the world
Models for automated, high-throughput plant phenotyping—measuring the physical characteristics of plants and crops, such as wheat head density and counts—are important tools for crop breeding (Thorp et al., [2018](#bib.bib372); Reynolds et al., [2020](#bib.bib313)) and agricultural field management (Shi et al., [2016](#bib.bib342)).
These models are typically trained on data collected in a limited number of regions, even for crops grown worldwide such as wheat (Madec et al., [2019](#bib.bib254); Xiong et al., [2019](#bib.bib417); Ubbens et al., [2020](#bib.bib381); Ayalew et al., [2020](#bib.bib22)).
However, there can be substantial variation between regions, due to differences in crop varieties, growing conditions, and data collection protocols.
Prior work on wheat head detection has shown that this variation can significantly degrade model performance on regions unseen during training (David et al., [2020](#bib.bib104)).
We study this shift in an expanded version of the Global Wheat Head Dataset (David et al., [2020](#bib.bib104), [2021](#bib.bib105)), a large set of wheat images collected from 12 countries around the world (Figure [7](#S4.F7 "Figure 7 ‣ 4.1.5 GlobalWheat-wilds: Wheat head detection across regions of the world ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
It is a detection dataset, where the input x𝑥xitalic\_x is a cropped overhead image of a wheat field, the label y𝑦yitalic\_y is the set of bounding boxes for each wheat head visible in the image, and the domain d𝑑ditalic\_d specifies an image acquisition session (i.e., a specific location, time, and sensor with which a set of images was collected).
The data split captures a shift in location, with training and test sets comprising images from disjoint countries.
As leverage, we include images from 18 acquisition sessions over 5 countries in the training set.
We evaluate model performance on unseen countries by measuring accuracy at a fixed Intersection over Union (IoU) threshold, and averaging across acquisition sessions to account for imbalances in the numbers of images in them.
Additional details are provided in Appendix [E.5](#S5.SS5 "E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Figure 7:
The GlobalWheat-wilds dataset consists of overhead images of wheat fields, annotated with bounding boxes of wheat heads. The goal is to detect and predict the bounding boxes of wheat heads, where images are from new acquisition sessions. A set of wheat images are collected in each acquisition session, each corresponding to a specific wheat field location, time, and sensor. While acquisition sessions vary along multiple axes, from the aforementioned factors to wheat growth stage to illumination conditions, the dataset split primarily captures a shift in location; test images are taken from countries unseen during training time. In this figure, we show images with bounding boxes from different acquisition sessions.
###
4.2 Subpopulation shift datasets
####
4.2.1 CivilComments-wilds: Toxicity classification across demographic identities
Automatic review of user-generated text is an important tool for moderating the sheer volume of text written on the Internet.
We focus here on the task of detecting toxic comments.
Prior work has shown that toxicity classifiers can pick up on biases in the training data and spuriously associate toxicity with the mention of certain demographics (Park et al., [2018](#bib.bib286); Dixon et al., [2018](#bib.bib112)).
These types of spurious correlations can significantly degrade model performance on particular subpopulations (Sagawa et al., [2020a](#bib.bib327)).
We study this problem on a variant of the CivilComments dataset (Borkan et al., [2019b](#bib.bib55)), a large collection of comments on online articles taken from the Civil Comments platform (Figure [8](#S4.F8 "Figure 8 ‣ 4.2.1 CivilComments-wilds: Toxicity classification across demographic identities ‣ 4.2 Subpopulation shift datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The input x𝑥xitalic\_x is a text comment, the label y𝑦yitalic\_y is whether the comment was rated as toxic, and the domain d𝑑ditalic\_d is a 8-dimensional binary vector where each component corresponds to whether the comment mentions one of the 8 demographic identities male, female, LGBTQ, Christian, Muslim, other religions, Black, and White.
The training and test sets comprise comments on disjoint articles, and we evaluate models by the lowest true positive/negative rate over each of these 8 demographic groups; these groups overlap with each other, deviating slightly from the standard subpopulation shift framework in Section [3](#S3 "3 Problem settings ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Models can use the provided domain annotations as leverage to learn to perform well over each demographic group.
Appendix [E.6](#S5.SS6 "E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
Figure 8:
The CivilComments-wilds dataset involves classifying the toxicity of online comments. The goal is to learn models that avoid spuriously associating mentions of demographic identities (like male, female, etc.) with toxicity due to biases in the training data.
###
4.3 Hybrid datasets
####
4.3.1 FMoW-wilds: Land use classification across different regions and years
ML models for satellite imagery can enable global-scale monitoring of sustainability and economic challenges, aiding policy and humanitarian efforts in applications such as deforestation tracking (Hansen et al., [2013](#bib.bib164)), population density mapping (Tiecke et al., [2017](#bib.bib374)), crop yield prediction (Wang et al., [2020b](#bib.bib395)), and other economic tracking applications (Katona et al., [2018](#bib.bib199)).
As satellite data constantly changes due to human activity and environmental processes, these models must be robust to distribution shifts over time.
Moreover, as there can be disparities in the data available between regions,
these models should ideally have uniformly high accuracies instead of only doing well on data-rich regions and countries.
We study this problem on a variant of the Functional Map of the World dataset (Christie et al., [2018](#bib.bib83)), where the input x𝑥xitalic\_x is an RGB satellite image, the label y𝑦yitalic\_y is one of 62 building or land use categories, and the domain d𝑑ditalic\_d represents the year the image was taken and its geographical region (Africa, the Americas, Oceania, Asia, or Europe) (Figure [9](#S4.F9 "Figure 9 ‣ 4.3.1 FMoW-wilds: Land use classification across different regions and years ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). The different regions have different numbers of examples, e.g., there are far fewer images from Africa than the Americas.
The training set comprises data from before 2013, while the test set comprises data from 2016 and after; years 2013 to 2015 are reserved for the validation set.
We evaluate models by their test accuracy on the worst geographical region, which combines both a domain generalization problem over time and a subpopulation shift problem over regions.
As we provide both time and region annotations, models can leverage the structure across both space and time to improve robustness.
Appendix [E.7](#S5.SS7 "E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
Figure 9:
The FMoW-wilds dataset contains satellite images taken in different geographical regions and at different times. The goal is to generalize to satellite imagery taken in the future, which may be shifted due to infrastructure development across time, and to do equally well across geographic regions.
####
4.3.2 PovertyMap-wilds: Poverty mapping across different countries
Global-scale poverty estimation is a specific remote sensing application which is essential for targeted humanitarian efforts in poor regions (Abelson et al., [2014](#bib.bib1); Espey et al., [2015](#bib.bib124)).
However, ground truth measurements of poverty are lacking for much of the developing world, as field surveys for collecting the ground truth are expensive (Blumenstock et al., [2015](#bib.bib51)).
This motivates the approach of training ML models on countries with ground truth labels and then deploying them on different countries where we have satellite data but no labels (Xie et al., [2016](#bib.bib415); Jean et al., [2016](#bib.bib187); Yeh et al., [2020](#bib.bib422)).
We study this shift through a variant of the poverty mapping dataset collected by Yeh et al. ([2020](#bib.bib422)), where the input x𝑥xitalic\_x is a multispectral satellite image, the output y𝑦yitalic\_y is a real-valued asset wealth index from surveys, and the domain d𝑑ditalic\_d represents the country the image was taken in and whether the image is of an urban or rural area (Figure [10](#S4.F10 "Figure 10 ‣ 4.3.2 PovertyMap-wilds: Poverty mapping across different countries ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). The training and test set comprise data from disjoint sets of countries, and we evaluate models by the correlation of their predictions with the ground truth. Specifically, we take the lower of the correlations over the urban and rural subpopulations, as prior work has shown that accurately predicting poverty within these subpopulations is especially challenging.
As poverty measures are highly correlated across space (Jean et al., [2018](#bib.bib188); Rolf et al., [2020](#bib.bib319)), methods can utilize the provided location coordinates, and the country and urban/rural annotations, to improve robustness.
Appendix [E.8](#S5.SS8 "E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
Figure 10: The PovertyMap-wilds dataset contains satellite images taken in different countries. The goal is to predict asset wealth in countries that are not present in the training set, while being accurate in both urban and rural areas. There may be significant economic and cultural differences across country borders that contribute to the spatial distribution shift.
Figure 11:
The Amazon-wilds dataset involves predicting star ratings from reviews of Amazon products. The goal is to do consistently well on new reviewers who are not in the training set.
####
4.3.3 Amazon-wilds: Sentiment classification across different users
In many consumer-facing ML applications, models are trained on data collected on one set of users and then deployed across a wide range of potentially new users.
These models can perform well on average but poorly on some users (Tatman, [2017](#bib.bib366); Caldas et al., [2018](#bib.bib72); Li et al., [2019b](#bib.bib235); Koenecke et al., [2020](#bib.bib208)).
These large performance disparities across users are practical concerns in consumer-facing applications, and they can also indicate that models are exploiting biases or spurious correlations in the data (Badgeley et al., [2019](#bib.bib24); Geva et al., [2019](#bib.bib146)).
We study this issue on a variant of the Amazon review dataset (Ni et al., [2019](#bib.bib274)), where the input x𝑥xitalic\_x is the review text, the label y𝑦yitalic\_y is the corresponding 1-to-5 star rating, and the domain d𝑑ditalic\_d identifies the user who wrote the review (Figure [11](#S4.F11 "Figure 11 ‣ 4.3.2 PovertyMap-wilds: Poverty mapping across different countries ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). The training and test sets comprise reviews from disjoint sets of users; for leverage, the training set has reviews from 5,008 different users. As our goal is to train models with consistently high performance across users, we evaluate models by the 10th percentile of per-user accuracies.
Appendix [E.9](#S5.SS9 "E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides additional details and context.
We discuss other distribution shifts on this dataset (e.g., by category) in Appendix [F.4](#S6.SS4a "F.4 Amazon: Sentiment classification across different categories and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
####
4.3.4 Py150-wilds: Code completion across different codebases
Code completion models—autocomplete tools used by programmers to suggest subsequent source code tokens, such as the names of API calls—are commonly used to reduce the effort of software development (Robbes and Lanza, [2008](#bib.bib317); Bruch et al., [2009](#bib.bib62); Nguyen and Nguyen, [2015](#bib.bib273); Proksch et al., [2015](#bib.bib300); Franks et al., [2015](#bib.bib132)).
These models are typically trained on data collected from existing codebases but then deployed more generally across other codebases, which may have different distributions of API usages (Nita and Notkin, [2010](#bib.bib275); Proksch et al., [2016](#bib.bib301); Allamanis and Brockschmidt, [2017](#bib.bib10)).
This shift across codebases can cause substantial performance drops in code completion models.
Moreover, prior studies of real-world usage of code completion models have noted that they can generalize poorly on some important subpopulations of tokens such as method names (Hellendoorn et al., [2019](#bib.bib170)).
We study a variant of the Py150 Dataset (Raychev et al., [2016](#bib.bib306); Lu et al., [2021](#bib.bib248)), where the goal is to predict the next token (e.g., "environ", "communicate" in Figure [12](#S4.F12 "Figure 12 ‣ 4.3.4 Py150-wilds: Code completion across different codebases ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")) given the context of previous tokens.
The input x𝑥xitalic\_x is a sequence of source code tokens, the label y𝑦yitalic\_y is the next token, and the domain d𝑑ditalic\_d specifies the repository that the source code belongs to.
The training and test sets comprise code from disjoint GitHub repositories.
As leverage, we include over 5,300 repositories in the training set, capturing a wide range of source code variation. We evaluate models by their accuracy on the subpopulation of class and method tokens.
Additional dataset and model details are provided in Appendix [E.10](#S5.SS10 "E.10 Py150-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Figure 12:
The Py150-wilds dataset comprises Python source code files taken from a variety of public repositories on GitHub. The task is code completion: predict token names given the context of previous tokens. We evaluate models on their accuracy on the subpopulation of API calls (i.e., method and class tokens), which are the most common code completion queries in real-world settings. Our goal is to learn code completion models that generalize to source code in new repositories that are not seen in the training set.
5 Performance drops from distribution shifts
---------------------------------------------
For a dataset to be appropriate for Wilds, the distribution shift reflected in its official train/test split should cause significant performance drops in standard models.
How to measure the performance drop due to a distribution shift is a crucial but subtle question.
In this section, we discuss our approach and the results on each of the Wilds datasets.
To construct Wilds, we selected datasets with large performance drops;
in Section [8](#S8 "8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we discuss other datasets with real-world shifts that did not show large performance drops and were therefore not included in the benchmark.
Our general approach is to measure the difference between the out-of-distribution (OOD) and in-distribution (ID) performance of standard models trained via empirical risk minimization (ERM).
Concretely, we first measure the OOD performance using the official train/test splits described in Section [4](#S4 "4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
We then construct an appropriate in-distribution (ID) setting to measure ID performance, typically by modifying the official train/test splits.
However, practical constraints often prevent us from constructing an ID setting in exactly the way we want, which makes the choice of appropriate ID setting for each dataset a case-by-case issue.
###
5.1 In-distribution performance should be measured on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, not P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT
Choosing an appropriate in-distribution (ID) setting is the crux of measuring how much a distribution shift affects performance.
But what distribution should “in-distribution” be taken with respect to?
Consider a distribution shift from a training distribution P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT to a test distribution P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
It is common to measure ID performance by taking a model trained on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and evaluating it on additional held-out data from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT.111For example, in domain generalization, we might train a model on the training domains and then report its ID performance on held-out examples from the same domains; and in subpopulation shift, we might report average performance on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT as the ID performance.
This is useful for checking if the model can generalize well on both the training and the shifted test distributions.
However, it fails to isolate the effect of the distribution shift since it does not control for the data distribution on which the model is evaluated: the ID setting evaluates on data from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT, whereas the OOD setting evaluates on data from P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
As a result, the performance gap might also be due to other factors such as differences in the difficulty of fitting a model to P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT versus P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
For illustration, consider the task of wheat head detection on GlobalWheat-wilds.
The shift from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT to P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, which contain images of wheat fields in Europe and North America respectively, involves changes in factors such as wheat genotype, illumination, and growing conditions.
These changes mean that the task can be more challenging in some regions than others:
for example, wheat is grown in higher densities in certain regions than others, and it is harder to detect wheat heads reliably when they are more densely packed together.
If, for example, the task is harder in the regions in P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, then we might see especially low performance on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT compared to P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT. However, this performance gap would overestimate the actual gap caused by the distribution shift, in the sense that performance on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT would still be lower even if we could train a model purely on data from P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
To isolate the gap caused by the distribution shift, it is therefore important to keep the evaluation data distribution fixed between the ID and OOD settings by evaluating on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT in the ID setting.
For example, we could measure ID performance by training on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT and evaluating on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT and then compare this with the standard OOD setting of training on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and evaluating on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
However, there is a practical drawback: we generally have much more data from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT rather than P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, and training and evaluating on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT would require us to have a substantial number of labeled examples from each test domain.
In contrast, the standard ID setting of training and evaluating on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT is typically much more feasible, and it is also more convenient as we can reuse the same model trained on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT for both ID and OOD evaluations.
In Wilds, we take the approach of measuring ID performance on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT whenever practically feasible, and we lean on standard ID evaluations on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT otherwise.
In either case, we generally provide held-out data from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT in order to track model performance on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT.
###
5.2 Types of in-distribution settings
To measure the performance drop on each Wilds dataset, we picked the most appropriate ID setting(s) that were feasible.
We now describe five specific ways of constructing ID settings and their pros and cons.
The first two ID settings (test-to-test and mixed-to-test) control for the evaluation distribution and thus isolate the performance drops due to distribution shifts, as discussed in Section [5.1](#S5.SS1 "5.1 In-distribution performance should be measured on 𝑃^𝗍𝖾𝗌𝗍, not 𝑃^𝗍𝗋𝖺𝗂𝗇 ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
However, these procedures require substantial training data from test domains, so in cases where such data is not practically available, we consider the other ID settings (train-to-train, average, and random split).
Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") describes dataset-specific rationales for the selected ID settings and additional details for each dataset.
Below, we denote the training and OOD test sets of the official Wilds splits as D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, sampled from distributions P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, respectively.
##### Test-to-test (train on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, test on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT).
To control for the evaluation distribution, we can hold the test set D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT fixed and train on a separate but identically-distributed training set D𝗁𝖾𝗅𝖽𝗈𝗎𝗍𝗍𝖾𝗌𝗍subscriptsuperscript𝐷𝗍𝖾𝗌𝗍𝗁𝖾𝗅𝖽𝗈𝗎𝗍D^{\mathsf{test}}\_{\mathsf{heldout}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT start\_POSTSUBSCRIPT sansserif\_heldout end\_POSTSUBSCRIPT drawn from P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
The ID performance reported in this setting is directly comparable to OOD performance, which is also evaluated on D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
The main drawback is that for a fair comparison to the OOD setting, where we train a model on D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT, we would require D𝗁𝖾𝗅𝖽𝗈𝗎𝗍𝗍𝖾𝗌𝗍subscriptsuperscript𝐷𝗍𝖾𝗌𝗍𝗁𝖾𝗅𝖽𝗈𝗎𝗍D^{\mathsf{test}}\_{\mathsf{heldout}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT start\_POSTSUBSCRIPT sansserif\_heldout end\_POSTSUBSCRIPT to match the size of D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT.
This is not feasible in our datasets, as D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT typically comprises the bulk of the available data.
We therefore do not use the test-to-test comparison for any of the Wilds datasets and instead consider the more practical alternative below, which still controls for the evaluation data distribution.
##### Mixed-to-test (train on a mixture of P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, test on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT).
In the mixed-to-test setting, we train a model on a mixture of data from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT and then evaluate it only on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
This is a more practical version of the test-to-test setting, as it retains the advantage of controlling for the evaluation distribution, while mitigating the need for large amounts of labeled data from P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT to use for training.222In practice, we typically split up D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT and use some of it for training by replacing examples in D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT (so that the size of the training set is similar to the OOD setting). This still requires D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT to be large enough to support using a sufficient number of examples for training while also having enough examples left over for accurate evaluation.
We use the mixed-to-test comparison for the Wilds datasets wherever feasible, except when we expect the train-to-train comparison to give similar results as described in the below discussion on train-to-train setting (e.g., for iWildCam2020-wilds and Py150-wilds).
One downside is that compared to the test-to-test setting, the mixed-to-test setting might underestimate ID performance, since it trains a model that simultaneously fits both P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, instead of just focusing on P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT.
However, this is useful as a sanity check that we can learn a model that can simultaneously fit both P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT; if such a model were not possible to learn, then it suggests that the distribution shift in the dataset is intractable for the model family.
##### Train-to-train (train on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT, evaluate on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT).
In the train-to-train setting, we train a model on D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and evaluate on a separate but identically-distributed test set D𝗁𝖾𝗅𝖽𝗈𝗎𝗍𝗍𝗋𝖺𝗂𝗇subscriptsuperscript𝐷𝗍𝗋𝖺𝗂𝗇𝗁𝖾𝗅𝖽𝗈𝗎𝗍D^{\mathsf{train}}\_{\mathsf{heldout}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT start\_POSTSUBSCRIPT sansserif\_heldout end\_POSTSUBSCRIPT drawn from P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT.
As discussed in Section [5.1](#S5.SS1 "5.1 In-distribution performance should be measured on 𝑃^𝗍𝖾𝗌𝗍, not 𝑃^𝗍𝗋𝖺𝗂𝗇 ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), this is practical—it does not require large amounts of data from P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, and we can reuse the model for OOD evaluation—but has the drawback of not controlling for the evaluation distribution.
This drawback is less of an issue when we expect D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT to be of equal difficulty in the sense of Section [5.1](#S5.SS1 "5.1 In-distribution performance should be measured on 𝑃^𝗍𝖾𝗌𝗍, not 𝑃^𝗍𝗋𝖺𝗂𝗇 ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
This may be the case when the dataset has a relatively large number of training and test domains that are drawn from the same distribution, and they are thus roughly interchangeable.
For instance, in iWildCam2020-wilds and Py150-wilds, there are many available domains (camera traps and GitHub repositories, respectively) randomly split across D𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝗋𝖺𝗂𝗇D^{\mathsf{train}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT and D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, so we use the train-to-train comparison for them.
For most of the other datasets, we also include train-to-train comparisons to track model performance on P𝗍𝗋𝖺𝗂𝗇superscript𝑃𝗍𝗋𝖺𝗂𝗇P^{\mathsf{train}}italic\_P start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT (i.e., the official splits typically also include a held-out D𝗁𝖾𝗅𝖽𝗈𝗎𝗍𝗍𝗋𝖺𝗂𝗇subscriptsuperscript𝐷𝗍𝗋𝖺𝗂𝗇𝗁𝖾𝗅𝖽𝗈𝗎𝗍D^{\mathsf{train}}\_{\mathsf{heldout}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT start\_POSTSUBSCRIPT sansserif\_heldout end\_POSTSUBSCRIPT; we report results on these in Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), but we complement them whenever feasible with other ID settings that better isolate the effect of the distribution shift.
##### Average (report average instead of worst-case performance).
In subpopulation shift datasets, we measure the OOD performance of a model by reporting the performance on the worst-case subpopulation, and we can measure ID performance by simply reporting the average performance.
This average comparison corresponds to a special case of the train-to-train setting,333In subpopulation shifts, the training distribution reflects the empirical make-up over the pre-defined subpopulations, whereas the test distribution of interest corresponds to the worst-case subpopulation.
so they share the same pros and cons.
In particular, the average comparison is much more practical than running a test-to-test comparison on each subpopulation, as it can be especially difficult to obtain sufficient training examples from minority subpopulations.
In Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we use this average comparison for the CivilComments-wilds and Amazon-wilds datasets, which both consider a large number of subpopulations that are individually quite small.
##### Random split (train and evaluate on an i.i.d. split).
Another standard approach to measuring ID performance is to shuffle all of the data in D𝗍𝗋𝖺𝗂𝗇∪D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝗋𝖺𝗂𝗇superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{train}}\cup D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT ∪ italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT into i.i.d. training, validation, and test splits, while keeping the size of the training set constant.
We use this in OGB-MolPCBA to be consistent with prior work from the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)).
As with the train-to-train comparison, the random split comparison is simple to implement and does not require large amounts of data from D𝗍𝖾𝗌𝗍superscript𝐷𝗍𝖾𝗌𝗍D^{\mathsf{test}}italic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT, but it does not control for the evaluation distribution.
###
5.3 Model selection
We used standard model architectures for each dataset: ResNet and DenseNet for images (He et al., [2016](#bib.bib167); Huang et al., [2017](#bib.bib183)), DistilBERT for text (Sanh et al., [2019](#bib.bib330)), a Graph Isomorphism Network (GIN) for graphs (Xu et al., [2018](#bib.bib418)), and Faster-RCNN (Ren et al., [2015](#bib.bib312)) for detection.
As our goal is high OOD performance,
we use a separate OOD validation set for early stopping and hyperparameter selection.444This means that while the ERM models do not make use of any additional metadata (e.g., domain annotations) during training, this metadata is still implicitly (but very mildly) used for model selection.
Relative to the training set, this OOD validation set reflects a distribution shift similar to, but distinct from, the test set.
For example, in iWildCam2020-wilds, the training, validation, and test sets each comprise photos from distinct sets of camera traps. We detail experimental protocol in Appendix [D](#S4a "D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and models and hyperparameters for each dataset in Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
For the ID comparisons, we use the same hyperparameters optimized on the OOD validation set, so our ID results are slightly lower than if we had optimized hyperparameters for ID performance (Appendix [D](#S4a "D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). In other words, the ID-OOD gaps in Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") are slightly underestimated.
###
5.4 Results
Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that for each dataset, OOD performance is consistently and substantially lower than the corresponding ID performance.
Moreover, on the datasets that allow for mixed-to-test ID comparisons,
we show that models trained on a mix of the ID and OOD distributions can simultaneously achieve high ID and OOD performance,
indicating that lower OOD performance is not due to the OOD test sets being intrinsically more difficult than the ID test sets.
Overall, these results demonstrate that the real-world distribution shifts reflected in the Wilds datasets meaningfully degrade standard model performance.
Additional results for datasets that admit multiple ID comparisons are described for each dataset in Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Table 1: The in-distribution (ID) vs. out-of-distribution (OOD) performance of models trained with empirical risk minimization.
The OOD test sets are drawn from the shifted test distributions described in Section [4](#S4 "4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"),
while the ID comparisons vary per dataset and are described in Section [5.1](#S5.SS1 "5.1 In-distribution performance should be measured on 𝑃^𝗍𝖾𝗌𝗍, not 𝑃^𝗍𝗋𝖺𝗂𝗇 ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
For each dataset, higher numbers are better.
In all tables in this paper, we report in parentheses the standard deviation across 3+ replicates, which measures the variability between replicates; note that this is higher than the standard error of the mean, which measures the variability in the estimate of the mean across replicates.
All datasets show performance drops due to distribution shift, with substantially better ID performance than OOD performance.
| | | | | | |
| --- | --- | --- | --- | --- | --- |
| Dataset | Metric | In-dist setting | In-dist | Out-of-dist | Gap |
| iWildCam2020-wilds | Macro F1 | Train-to-train | 47.0 (1.4) | 31.0 (1.3) | 16.0 |
| Camelyon17-wilds | Average acc | Train-to-train | 93.2 (5.2) | 70.3 (6.4) | 22.9 |
| RxRx1-wilds | Average acc | Mixed-to-test | 39.8 (0.2) | 29.9 (0.4) | 9.9 |
| OGB-MolPCBA | Average AP | Random split | 34.4 (0.9) | 27.2 (0.3) | 7.2 |
| GlobalWheat-wilds | Average domain acc | Mixed-to-test | 63.3 (1.7) | 49.6 (1.9) | 13.7 |
| CivilComments-wilds | Worst-group acc | Average | 92.2 (0.1) | 56.0 (3.6) | 36.2 |
| FMoW-wilds | Worst-region acc | Mixed-to-test | 48.6 (0.9) | 32.3 (1.3) | 16.3 |
| PovertyMap-wilds | Worst-U/R Pearson R | Mixed-to-test | 0.60 (0.06) | 0.45 (0.06) | 0.15 |
| Amazon-wilds | 10th percentile acc | Average | 71.9 (0.1) | 53.8 (0.8) | 18.1 |
| Py150-wilds | Method/class acc | Train-to-train | 75.4 (0.4) | 67.9 (0.1) | 7.5 |
Table 2: The out-of-distribution test performance of models trained with different baseline algorithms: CORAL, originally designed for unsupervised domain adaptation; IRM, for domain generalization; and Group DRO, for subpopulation shifts. Evaluation metrics for each dataset are the same as in Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"); higher is better.
Overall, these algorithms did not improve over empirical risk minimization (ERM), and sometimes made performance significantly worse, except on CivilComments-wilds where they perform better but still do not close the in-distribution gap in Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
For GlobalWheat-wilds, we omit CORAL and IRM as those methods do not port straightforwardly to detection settings; its ERM number also differs from Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") as its ID comparison required a slight change to the OOD test set.
Parentheses show standard deviation across 3+ replicates.
| | | | | | |
| --- | --- | --- | --- | --- | --- |
| Dataset | Setting | ERM | CORAL | IRM | Group DRO |
| iWildCam2020-wilds | Domain gen. | 31.0 (1.3) | 32.8 (0.1) | 15.1 (4.9) | 23.9 (2.1) |
| Camelyon17-wilds | Domain gen. | 70.3 (6.4) | 59.5 (7.7) | 64.2 (8.1) | 68.4 (7.3) |
| RxRx1-wilds | Domain gen. | 29.9 (0.4) | 28.4 (0.3) | 8.2 (1.1) | 23.0 (0.3) |
| OGB-MolPCBA | Domain gen. | 27.2 (0.3) | 17.9 (0.5) | 15.6 (0.3) | 22.4 (0.6) |
| GlobalWheat-wilds | Domain gen. | 51.2 (1.8) | — | — | 47.9 (2.0) |
| CivilComments-wilds | Subpop. shift | 56.0 (3.6) | 65.6 (1.3) | 66.3 (2.1) | 70.0 (2.0) |
| FMoW-wilds | Hybrid | 32.3 (1.3) | 31.7 (1.2) | 30.0 (1.4) | 30.8 (0.8) |
| PovertyMap-wilds | Hybrid | 0.45 (0.06) | 0.44 (0.06) | 0.43 (0.07) | 0.39 (0.06) |
| Amazon-wilds | Hybrid | 53.8 (0.8) | 52.9 (0.8) | 52.4 (0.8) | 53.3 (0.0) |
| Py150-wilds | Hybrid | 67.9 (0.1) | 65.9 (0.1) | 64.3 (0.2) | 65.9 (0.1) |
6 Baseline algorithms for distribution shifts
----------------------------------------------
Many algorithms have been proposed for training models that are more robust to particular distribution shifts than standard models trained by empirical risk minimization (ERM), which trains models to minimize the average training loss.
Unlike ERM, these algorithms tend to utilize domain annotations during training, with the goal of learning a model that can generalize across domains.
In this section, we evaluate several representative algorithms from prior work and show that the out-of-distribution performance drops shown in Section [5](#S5 "5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") still remain.
###
6.1 Domain generalization baselines
Methods for domain generalization typically involve adding a penalty to the ERM objective that encourages some form of invariance across domains.
We include two such methods as representatives:
* •
CORAL (Sun and Saenko, [2016](#bib.bib356)), which penalizes differences in the means and covariances of the feature distributions (i.e., the distribution of last layer activations in a neural network) for each domain.
Conceptually, CORAL is similar to other methods that encourage feature representations to have the same distribution across domains
(Tzeng et al., [2014](#bib.bib380); Long et al., [2015](#bib.bib246); Ganin et al., [2016](#bib.bib137); Li et al., [2018c](#bib.bib237), [b](#bib.bib233)).
* •
IRM (Arjovsky et al., [2019](#bib.bib16)), which penalizes feature distributions that have different optimal linear classifiers for each domain. This builds on earlier work on invariant predictors (Peters et al., [2016](#bib.bib293)).
Other techniques for domain generalization include
conditional variance regularization (Heinze-Deml and Meinshausen, [2017](#bib.bib169));
self-supervision (Carlucci et al., [2019](#bib.bib76));
and meta-learning-based approaches (Li et al., [2018a](#bib.bib230); Balaji et al., [2018](#bib.bib25); Dou et al., [2019](#bib.bib115)).
###
6.2 Subpopulation shift baselines
In subpopulation shift settings, our aim is to train models that perform well on all relevant subpopulations. We test the following approach:
* •
Group DRO (Hu et al., [2018](#bib.bib181); Sagawa et al., [2020a](#bib.bib327)), which uses distributionally robust optimization to explicitly minimize the loss on the worst-case domain during training. Group DRO builds on the maximin approach developed in Meinshausen and Bühlmann ([2015](#bib.bib263)).
Other methods for subpopulation shifts include
reweighting methods based on class/domain frequencies (Shimodaira, [2000](#bib.bib343); Cui et al., [2019](#bib.bib100));
label-distribution-aware margin losses (Cao et al., [2019](#bib.bib75));
adaptive Lipschitz regularization (Cao et al., [2020](#bib.bib74));
slice-based learning (Chen et al., [2019b](#bib.bib81); Ré et al., [2019](#bib.bib307));
style transfer across domains (Goel et al., [2020](#bib.bib149));
or other DRO algorithms that do not make use of explicit domain information and
rely on, for example, unsupervised clustering (Oren et al., [2019](#bib.bib281); Sohoni et al., [2020](#bib.bib348))
or upweighting high-loss points (Nam et al., [2020](#bib.bib270); Liu et al., [2021a](#bib.bib241)).
Subpopulation shifts are also connected to the well-studied notions of tail performance and risk-averse optimization (Chapter 6 in Shapiro et al. ([2014](#bib.bib338))).
For example, optimizing for the worst case over all subpopulations of a certain size, regardless of domain, can guarantee a certain level of performance over the smaller set of subpopulations defined by domains (Duchi et al., [2020](#bib.bib119); Duchi and Namkoong, [2021](#bib.bib118)).
###
6.3 Setup
We trained CORAL, IRM, and Group DRO models on each dataset.
While Group DRO was originally developed for subpopulation shifts, for completeness, we also experiment with using it for domain generalization. In that setting, Group DRO models aim to achieve similar performance across domains: e.g., in Camelyon17-wilds, where the domains are hospitals, Group DRO optimizes for the training hospital with the highest loss.
Similarly, we also test CORAL and IRM on subpopulation shifts, where they encourage models to learn invariant representations across subpopulations.
As in Section [5](#S5 "5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we used the same OOD validation set for early stopping and to tune the penalty weights for the CORAL and IRM algorithms.
More experimental details are in Appendix [D](#S4a "D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), and dataset-specific hyperparameters and domain choices are discussed in Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
6.4 Results
Table [2](#S5.T2 "Table 2 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that models trained with CORAL, IRM, and Group DRO generally fail to improve over models trained with ERM.
The exception is the CivilComments-wilds subpopulation shift dataset, where the worst-performing subpopulation is a minority domain. By upweighting the minority domain, Group DRO obtains an OOD accuracy of 70.0% (on the worst-performing subpopulation) compared to 56.0% for ERM, though this is still substantially below the ERM model’s ID accuracy of 92.2% (on average over the entire test set). CORAL and IRM also perform well on CivilComments-wilds, though the gains there stem from the fact that our implementation heuristically upsamples the minority domain (see Appendix [E.6](#S5.SS6 "E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
All other datasets involve domain generalization; the failure of the baseline algorithms here is consistent with other recent findings on standard domain generalization datasets (Gulrajani and Lopez-Paz, [2020](#bib.bib158)).
These results indicate that training models to be robust to distribution shifts in the wild remains a significant open challenge. However, we are optimistic about future progress for two reasons.
First, current methods were mostly designed for other problem settings besides domain generalization, e.g., CORAL for unsupervised domain adaptation and Group DRO for subpopulation shifts.
Second, compared to existing distribution shift datasets, the Wilds datasets generally contain diverse training data from many more domains as well as metadata on these domains, which future algorithms might be able to leverage.
7 Empirical trends
-------------------
We end our discussion of experimental results by briefly reporting on several trends that we observed across multiple datasets.
###
7.1 Underspecification
Prior work has shown that there is often insufficient information at training time to distinguish models that would generalize well under distribution shift;
many models that perform similarly in-distribution (ID) can vary substantially out-of-distribution (OOD) (McCoy et al., [2019a](#bib.bib259); Zhou et al., [2020](#bib.bib433); D’Amour et al., [2020a](#bib.bib102)).
In Wilds, we attempt to alleviate this issue by providing multiple training domains in each dataset as well as an OOD validation set for model selection.
Perhaps as a result, we do not observe significantly higher variance in OOD performance than ID performance in Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), with the exception of
Amazon-wilds and CivilComments-wilds, where the OOD performance is measured on a smaller subpopulation and is therefore naturally more variable.
Excluding those datasets, the average standard deviation from Table [1](#S5.T1 "Table 1 ‣ 5.4 Results ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") is 2.6% for OOD performance and 2.0% for ID performance, which is comparable.
These results raise the question of when underspecification, as reported in prior work, could be more of an issue.
###
7.2 Model selection with in-distribution versus out-of-distribution validation sets
All of the baseline results reported in this paper use an OOD validation set for model selection, as discussed in Section [5.3](#S5.SS3 "5.3 Model selection ‣ 5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
To facilitate research into comparisons of ID versus OOD performance, most Wilds datasets also provide an ID validation and/or test set.
For example, in iWildCam2020-wilds, the ID validation set comprises photos from the same set of camera traps used for the training set.
These ID sets are not used for model selection nor official evaluation.
Gulrajani and Lopez-Paz ([2020](#bib.bib158)) showed that on the DomainBed domain generalization datasets, selecting models with an ID validation set leads to higher OOD performance than using an OOD validation set.
This contrasts with our approach of using OOD validation sets, which we find to generally provide a good estimate of OOD test performance.
Specifically, in Appendix [D.1](#S4.SS1a "D.1 Model hyperparameters ‣ D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we show that for our baseline models, model selection using an OOD validation set results in comparable or higher OOD performance than model selection using an ID validation set.
This difference could stem from many factors: for example, Wilds datasets tend to have many more domains, whereas DomainBed datasets tend to have fewer domains that can be quite different from each other (e.g., cartoons vs. photos);
and there are some differences in the exact procedures for comparing performance using ID versus OOD validation sets.
Further study of the effects of these different model selection procedures and choices of validation sets would be a useful direction for future work.
###
7.3 The compounding effects of multiple distribution shifts
Several Wilds datasets consider hybrid settings, where the goal is to simultaneously generalize to unseen domains as well as to certain subpopulations.
We observe that combining these types of shifts can exacerbate performance drops.
For example, in PovertyMap-wilds and FMoW-wilds, the shift to unseen domains exacerbates the gap in subpopulation performance (and vice versa).
Notably, in FMoW-wilds, the difference in subpopulation performance (across regions) is not even manifested until also considering another shift (across time).
While we do not always observe the compounding effect of distribution shifts—e.g., in Amazon-wilds, subpopulation performance is similar whether we consider shifts to unseen users or not—these observations underscore the importance of evaluating models on the combination of distribution shifts that would occur in practice, instead of considering each shift in isolation.
8 Distribution shifts in other application areas
-------------------------------------------------
Beyond the datasets currently included in Wilds,
there are many other applications where it is critical for models to be robust to distribution shifts.
In this section, we discuss some of these applications and the challenges of finding appropriate benchmark datasets in those areas.
We also highlight examples of datasets with distribution shifts that we considered but did not include in Wilds, because their distribution shifts did not lead to a significant performance drop.
Constructing realistic benchmarks that reflect distribution shifts in these application areas is an important avenue of future work,
and we would highly welcome community contributions of benchmark datasets in these areas.
###
8.1 Algorithmic fairness
Distribution shifts which degrade model performance on minority subpopulations are frequently discussed in the algorithmic fairness literature.
Geographic inequities are one concern (Shankar et al., [2017](#bib.bib336); Atwood et al., [2020](#bib.bib19)): e.g., publicly available image datasets overrepresent images from the US and Europe, degrading performance in the developing world (Shankar et al., [2017](#bib.bib336)) and prompting the creation of more geographically diverse datasets (Atwood et al., [2020](#bib.bib19)).
Racial disparities are another concern: e.g., commercial gender classifiers are more likely to misclassify the gender of darker-skinned women, likely in part because training datasets overrepresent lighter-skinned subjects (Buolamwini and Gebru, [2018](#bib.bib67)), and pedestrian detection systems fare worse on darker-skinned pedestrians (Wilson et al., [2019](#bib.bib404)). As in Section [4.2.1](#S4.SS2.SSS1 "4.2.1 CivilComments-wilds: Toxicity classification across demographic identities ‣ 4.2 Subpopulation shift datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), NLP models can also show racial bias.
Unfortunately, publicly available algorithmic fairness benchmarks (Mehrabi et al., [2019](#bib.bib262))—e.g., the COMPAS recidivism dataset (Larson et al., [2016](#bib.bib223))—suffer from several limitations.
First, the datasets are often quite small by the standards of modern ML: the COMPAS dataset has only a few thousand rows (Larson et al., [2016](#bib.bib223)).
Second, they tend to have relatively few features,
and disparities in subgroup performance are not always large (Larrazabal et al., [2020](#bib.bib222)),
limiting the benefit of more sophisticated approaches:
on COMPAS, logistic regression performs comparably to a black-box commercial algorithm (Jung et al., [2020](#bib.bib194); Dressel and Farid, [2018](#bib.bib117)).
Third, the datasets sometimes represent “toy” problems: e.g., the UCI Adult Income dataset (Asuncion and Newman, [2007](#bib.bib17)) is widely used as a fairness benchmark, but its task—classifying whether a person will have an income above $50,000—does not represent a real-world application.
Finally, because many of the domains in which algorithmic fairness is of most concern—e.g., criminal justice and healthcare—are high-stakes and disparities are politically sensitive, it can be difficult to make datasets publicly available.
Creating algorithmic fairness benchmarks which do not suffer from these limitations represents a promising direction for future work. In particular, such datasets would ideally have: 1) information about a sensitive attribute like race or gender; 2) a prediction task which is of immediate real-world interest; 3) enough samples, a rich enough feature set, and large enough disparities in group performance that more sophisticated machine learning approaches would plausibly produce improvement over naive approaches.
##### Dataset: New York stop-and-frisk.
Predictive policing is a prominent example of a real-world application where fairness considerations are paramount:
algorithms are increasingly being used in contexts such as predicting crime hotspots (Lum and Isaac, [2016](#bib.bib249)) or a defendant’s risk of reoffending
(Larson et al., [2016](#bib.bib223); Corbett-Davies et al., [2016](#bib.bib93), [2017](#bib.bib94); Lum and Shah, [2019](#bib.bib250)).
There are numerous concerns about these applications (Larson et al., [2016](#bib.bib223); Corbett-Davies et al., [2016](#bib.bib93), [2017](#bib.bib94); Lum and Shah, [2019](#bib.bib250)),
one of which is that these ML models might not generalize beyond the distributions that they were trained on (Corbett-Davies and Goel, [2018](#bib.bib92); Slack et al., [2019](#bib.bib347)).
These distribution shifts include shifts over locations—e.g., a criminal risk assessment trained on several hundred defendants in Ohio was eventually used throughout the United States (Latessa et al., [2010](#bib.bib224))—and shifts over time, as sentencing and other criminal justice policies evolve (Corbett-Davies and Goel, [2018](#bib.bib92)).
There are, of course, also subpopulation shift concerns around whether models are biased against particular demographic groups.
We investigated these shifts using a dataset of pedestrian stops made by the New York City Police Department under its “stop-and-frisk” policy,
where the task is to predict whether a pedestrian who was stopped on suspicion of weapon possession would in fact possess a weapon (Goel et al., [2016](#bib.bib150)).
This policy had a pronounced racial bias: Black people stopped by the police on suspicion of possessing a weapon were 5×\times× less likely to actually possess one than their White counterparts (Goel et al., [2016](#bib.bib150)).
We emphasize that we oppose stop-and-frisk (and any “improved” ML-powered stop-and-frisk) since there is overwhelming evidence that the policy was racially discriminatory (Gelman et al., [2007](#bib.bib145); Goel et al., [2016](#bib.bib150); Pierson et al., [2018](#bib.bib296)) and such massive inequities require more than algorithmic fixes.
Rather, we use the dataset as a realistic example of the phenomena that arise in real policing contexts, including 1) substantial heterogeneity across locations and racial groups and 2) distributions that arise in part because of biased policing practices.
Overall, we found large performance disparities across race groups and locations. Interestingly, however, we also found that these disparities cannot be attributed to the distribution shift, as the disparities were not reduced when we trained models specifically on the race groups or locations that suffer the worst performance.
Indeed, the groups that see the worst performance—Black and Hispanic pedestrians—comprise large *majorities* of the dataset, making up more than 90% of the stops. This contrasts with the typical setting in algorithmic fairness where models perform worse on *minority* groups in the training data.
Our results suggest the disparities are due to the dataset being noisier for some race and location groups, potentially as a result of the biased policing practices underlying the dataset. We provide further details in Appendix [F.1](#S6.SS1a "F.1 SQF: Criminal possession of weapons across race and locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
8.2 Medicine and healthcare
Substantial evidence indicates the potential for distribution shifts in medical settings (Finlayson et al., [2021](#bib.bib131)). One concern is *demographic* subpopulation shifts (e.g., across race, gender, or socioeconomic status), since historically-disadvantaged populations are underrepresented in many medical datasets (Chen et al., [2020](#bib.bib79)).
Another concern is heterogeneity *across hospitals*; this might include differences in imaging, as in Section [4.1.2](#S4.SS1.SSS2 "4.1.2 Camelyon17-wilds: Tumor identification across different hospitals ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), and other operational protocols such as lab tests (D’Amour et al., [2020a](#bib.bib102); Subbaswamy et al., [2020](#bib.bib355)).
Finally, changes *over time* can also produce distribution shifts: for example, Nestor et al. ([2019](#bib.bib272)) showed that switching between two electronic health record (EHR) systems produced a drop in performance,
and the COVID-19 epidemic has affected the distribution of chest radiographs (Wong et al., [2020](#bib.bib407)).
Creating medical distribution shift benchmarks thus represents a promising direction for future work, if several challenges can be overcome. First, while there are large demographic disparities in healthcare outcomes (e.g., by race or socioeconomic status), many of them are not due to distribution shifts, but to disparities in non-algorithmic factors (e.g., access to care or prevalence of comorbidities (Chen et al., [2020](#bib.bib79))) or to algorithmic problems unrelated to distribution shift (e.g., choice of a biased outcome variable (Obermeyer et al., [2019](#bib.bib280))).
Indeed, several previous investigations have found relatively small disparities in algorithmic performance (as opposed to healthcare outcomes) across demographic groups (Chen et al., [2019a](#bib.bib78); Larrazabal et al., [2020](#bib.bib222)); Seyyed-Kalantari et al. ([2020](#bib.bib334)) finds larger disparities in true positive rates across demographic groups, but this might reflect the different underlying label distributions between groups.
Second, many distribution shifts in medicine arise from concept drifts, in which the relationship between the input and the label changes, for example due to changes in clinical procedures and the definition of the label (Widmer and Kubat, [1996](#bib.bib402); Beyene et al., [2015](#bib.bib46); Futoma et al., [2020](#bib.bib134)). It can be difficult to ensure that a potential benchmark has sufficient leverage for models to learn how to handle, e.g., an abrupt change in the way a particular clinical procedure is carried out.
A last challenge is data availability, as stringent medical privacy laws often preclude data sharing (Price and Cohen, [2019](#bib.bib299)). For example, EHR datasets are fundamental to medical decision-making, but there are few widely adopted EHR benchmarks—with the MIMIC database being a prominent exception (Johnson et al., [2016](#bib.bib190))—and relatively little progress in predictive performance has been made on them (Bellamy et al., [2020](#bib.bib41)).
###
8.3 Genomics
Advances in high-throughput genomic and molecular profiling platforms have enabled systematic mapping of biochemical activity of genomes across diverse cellular contexts, populations, and species
(Consortium et al., [2012](#bib.bib89); Ho et al., [2014](#bib.bib177); Kundaje et al., [2015](#bib.bib216); Regev et al., [2017](#bib.bib309); Consortium, [2019](#bib.bib91); Moore et al., [2020](#bib.bib268); Consortium et al., [2020](#bib.bib90)).
These datasets have powered ML models that have been fairly successful at deciphering functional DNA sequence patterns and predicting the consequences of genetic perturbations in cell types in which the models are trained (Libbrecht and Noble, [2015](#bib.bib239); Zhou and Troyanskaya, [2015](#bib.bib432); Kelley et al., [2016](#bib.bib203); Ching et al., [2018](#bib.bib82); Eraslan et al., [2019](#bib.bib123); Jaganathan et al., [2019](#bib.bib186); Avsec et al., [2021b](#bib.bib21)).
However, distribution shifts pose a significant obstacle to generalizing these predictions to new cell types.
A concrete example is the prediction of genome-wide profiles of regulatory protein-DNA binding interactions across cell types and tissues (Srivastava and Mahony, [2020](#bib.bib350)).
These regulatory maps are critical for understanding the fundamental mechanisms of dynamic gene regulation across healthy and diseased cell states, and predictive models are an essential complement to experimental approaches for comprehensively profiling these maps.
Regulatory proteins bind regulatory DNA elements in a sequence-specific manner to orchestrate gene expression programs.
These proteins often form different complexes with each other in different cell types.
These cell-type-specific protein complexes can recognize distinct combinatorial sequence syntax and thereby bind to different genomic locations in different cell types, even if all of these cell types share the same genomic sequence.
Hence, ML models that aim to predict protein-DNA binding landscapes across cell types typically integrate DNA sequence and additional context-specific input data modalities, which provide auxiliary information about the regulatory state of DNA in each cell type (Srivastava and Mahony, [2020](#bib.bib350)).
The training cell-type specific sequence determinants of binding induce a distribution shift across cell types, which can in turn degrade model performance on new cell types (Balsubramani et al., [2017](#bib.bib26); Li et al., [2019a](#bib.bib232); Li and Guan, [2019](#bib.bib231); Keilwagen et al., [2019](#bib.bib202); Quang and Xie, [2019](#bib.bib303)).
##### Dataset: Genome-wide protein-DNA binding profiles across different cell types.
We studied the above problem in the context of the ENCODE-DREAM in-vivo Transcription Factor Binding Site Prediction Challenge (Balsubramani et al., [2020](#bib.bib27)),
which is an open community challenge introduced to systematically benchmark ML models for predicting genome-wide DNA binding maps of many regulatory proteins across cell types.
For each regulatory protein, regions of the genome are associated with binary labels (bound/unbound).
The task is to predict these binary binding labels as a function of underlying DNA sequence and chromatin accessibility signal (an experimental measure of cell type-specific regulatory state) in test cell types that are not represented in the training set.
A systematic evaluation of the top-performing models in this challenge highlighted a significant gap in prediction performance across cell types, relative to cross-validation performance within training cell types (Li et al., [2019a](#bib.bib232); Li and Guan, [2019](#bib.bib231); Keilwagen et al., [2019](#bib.bib202); Quang and Xie, [2019](#bib.bib303)).
This performance gap was attributed to distribution shifts across cell types, due to regulatory proteins forming cell-type-specific complexes that can recognize different combinatorial sequence syntax.
Hence, the same DNA sequence can be associated with different binding labels for a protein across contexts.
We investigated these distribution shifts in more detail for a restricted subset of the challenge’s prediction tasks for two regulatory proteins, using a total of 14 genome-wide binding maps across different cell types.
While we generally found a performance gap between in- and out-of-distribution settings, we did not include this dataset in the official benchmark for several reasons.
For example, we were unable to learn a model that could generalize across all the cell types simultaneously, even in an in-distribution setting,
which suggested that the model family and/or feature set might not be rich enough to fit the variation across different cell types.
Another major complication was the significant variation in intrinsic difficulty across different splits, as measured by the performance of models we train in-distribution.
Further work will be required to construct a rigorous benchmark for evaluating distribution shifts in the context of predicting regulatory binding maps.
We discuss details in Appendix [F.2](#S6.SS2a "F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
8.4 Natural language and speech processing
Subpopulation shifts are an issue in automated speech recognition (ASR) systems, which have been shown to have higher error rates for Black speakers than for White speakers (Koenecke et al., [2020](#bib.bib208)) and for speakers of some dialects (Tatman, [2017](#bib.bib366)).
These disparities were demonstrated using commercial ASR systems, and therefore do not have any accompanying training datasets that are publicly available.
There are many public speech datasets with speaker metadata that could potentially be used to construct a benchmark, e.g., LibriSpeech (Panayotov et al., [2015](#bib.bib284)),
the Speech Accent Archive (Weinberger, [2015](#bib.bib398)),
VoxCeleb2 (Chung et al., [2018](#bib.bib84)),
the Spoken Wikipedia Corpus (Baumann et al., [2019](#bib.bib31)),
and Common Voice (Ardila et al., [2020](#bib.bib15)).
However, these datasets have their own challenges: some do not have a sufficiently diverse sample of speaker backgrounds and accents, and others focus on read speech (e.g., audiobooks) instead of more natural speech.
In natural language processing (NLP), a current focus is on challenge datasets that are crafted to test particular aspects of models,
e.g., HANS (McCoy et al., [2019b](#bib.bib260)), PAWS (Zhang et al., [2019](#bib.bib430)),
and CheckList (Ribeiro et al., [2020](#bib.bib314)).
These challenge datasets are drawn from test distributions that are often (deliberately) quite different from the data distributions that models are typically trained on.
Counterfactually-augmented datasets (Kaushik et al., [2019](#bib.bib200)) are a related type of challenge dataset where the training data is modified to make spurious correlates independent of the target, which can result in more robust models.
Others have studied train/test sets that are drawn from different sources, e.g., Wikipedia, Reddit, news articles, travel reviews, and so on (Oren et al., [2019](#bib.bib281); Miller et al., [2020](#bib.bib264); Kamath et al., [2020](#bib.bib198)).
Several synthetic datasets have also been designed to test compositional generalization, such as CLEVR (Johnson et al., [2017](#bib.bib191)), SCAN (Lake and Baroni, [2018](#bib.bib218)), and COGS (Kim and Linzen, [2020](#bib.bib205)). The test sets in these datasets are chosen such that models need to generalize to novel combinations of parts of training examples, e.g., familiar primitives and grammatical roles (Kim and Linzen, [2020](#bib.bib205)).
CLEVR is a visual question-answering (VQA) dataset; other examples of VQA datasets that are formulated as challenge datasets are the VQA-CP v1 and v2 datasets (Agrawal et al., [2018](#bib.bib3)), which create subpopulation shifts by intentionally altering the distribution of answers per question type between the train and test splits.
These NLP examples involve English-language models; other languages typically have fewer and smaller datasets available for training and benchmarking models.
Multi-lingual models and benchmarks (Conneau et al., [2018](#bib.bib88); Conneau and Lample, [2019](#bib.bib87); Hu et al., [2020a](#bib.bib180); Clark et al., [2020](#bib.bib85)) are another source of subpopulation shifts with corresponding disparities in performance:
training sets might contain fewer examples in low-resource languages (Nekoto et al., [2020](#bib.bib271)),
but we would still hope for high model performance on these minority groups.
##### Datasets: Other distribution shifts in Amazon and Yelp reviews.
In addition to user shifts on the Amazon Reviews dataset (Ni et al., [2019](#bib.bib274)), we also looked at category and time shifts on the same dataset, as well as user and time shifts on the Yelp Open Dataset555<https://www.yelp.com/dataset>.
However, for many of those shifts, we only found modest performance drops.
We provide additional details on Amazon in Appendix [F.4](#S6.SS4a "F.4 Amazon: Sentiment classification across different categories and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and on Yelp in Appendix [F.5](#S6.SS5 "F.5 Yelp: Sentiment classification across different users and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
8.5 Education
ML models can help in educational settings in a variety of ways:
e.g., assisting in grading (Piech et al., [2013](#bib.bib295); Shermis, [2014](#bib.bib340); Kulkarni et al., [2014](#bib.bib214); Taghipour and Ng, [2016](#bib.bib364)),
estimating student knowledge (Desmarais and Baker, [2012](#bib.bib109); Wu et al., [2020](#bib.bib410)),
identifying students who need help (Ahadi et al., [2015](#bib.bib4)),
or automatically generating explanations (Williams et al., [2016](#bib.bib403); Wu et al., [2019a](#bib.bib409)).
However, there are substantial distribution shifts in these settings as well.
For example, automatic essay scoring has been found to be affected by rater bias (Amorim et al., [2018](#bib.bib13)) and spurious correlations like essay length (Perelman, [2014](#bib.bib292)),
leading to problems with subpopulation shift.
Ideally, these systems would also generalize across different contexts, e.g., a model for scoring grammar should work well across multiple different essay prompts.
Recent attempts at predicting grades algorithmically (BBC, [2020](#bib.bib32); Broussard, [2020](#bib.bib61)) have also been found to be biased against certain subpopulations.
Unfortunately, there is a general lack of standardized education datasets, in part due to student privacy concerns and the proprietary nature of large-scale standardized tests.
Datasets from massive open online courses are a potential source of large-scale data (Kulkarni et al., [2015](#bib.bib213)).
In general, dataset construction for ML in education is an active area—e.g.,
the NeurIPS 2020 workshop on Machine Learning for Education666<https://www.ml4ed.org/>
has a segment devoted to finding “ImageNets for education”—and we hope to be able to include one in the future.
###
8.6 Robotics
Robot learning has emerged as a strong paradigm for automatically acquiring complex and skilled
behaviors such as locomotion (Yang et al., [2019](#bib.bib420); Peng et al., [2020](#bib.bib291)), navigation (Mirowski et al., [2017](#bib.bib267); Kahn et al., [2020](#bib.bib196)),
and manipulation (Gu et al., [2017](#bib.bib157); et al, [2019](#bib.bib126)). However, the advent of learning-based techniques for
robotics has not convincingly addressed, and has perhaps even exasperated, problems stemming from
distribution shift. These problems have manifested in many ways, including shifts induced by weather
and lighting changes (Wulfmeier et al., [2018](#bib.bib413)), location changes (Gupta et al., [2018](#bib.bib160)), and the
simulation-to-real-world gap (Sadeghi and Levine, [2017](#bib.bib323); Tobin et al., [2017](#bib.bib375)).
Dealing with these challenging
scenarios is critical to deploying robots in the real world, especially in high-stakes
decision-making scenarios.
For example, to safely deploy autonomous driving vehicles, it is critical that these systems work
reliably and robustly across the huge variety of conditions that exist in the real world, such as
locations, lighting and weather conditions, and sensor intrinsics. This is a challenging
requirement, as many of these conditions may be underrepresented, or not represented at all, by the
available training data. Indeed, prior work has shown that naively trained models can suffer at
segmenting nighttime driving scenes (Dai and Van Gool, [2018](#bib.bib101)), detecting relevant objects in new or
challenging locations and settings (Yu et al., [2020](#bib.bib424); Sun et al., [2020a](#bib.bib358)), and, as discussed earlier, detecting
pedestrians with darker skin tones (Wilson et al., [2019](#bib.bib404)).
Creating a benchmark for distribution shifts in robotics applications, such as autonomous driving,
represents a promising direction for future work. Here, we briefly summarize our initial findings on
distribution shifts in the BDD100K driving dataset (Yu et al., [2020](#bib.bib424)), which is publicly available and
widely used, including in some of the works listed above.
##### Dataset: BDD100K.
We investigated the task of multi-label binary classification of the presence of each object
category in each image. In general, we found no substantial performance drops across a wide range of
different test scenarios, including user shifts, weather and time shifts, and location shifts. We
provide additional details in Section [F.3](#S6.SS3a "F.3 BDD100K: Object recognition in autonomous driving across locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Our findings contrast with previous findings that other tasks, such as object detection and
segmentation, can suffer under the same types of shifts on the same dataset
(Yu et al., [2020](#bib.bib424); Dai and Van Gool, [2018](#bib.bib101)). Currently, Wilds consists of datasets involving classification and
regression tasks. However, most tasks of interest in autonomous driving, and robotics in general,
are difficult to formulate as classification or regression. For example, autonomous driving
applications may require models for object detection or lane and scene segmentation. These tasks are
often more challenging than classification tasks, and we speculate that they may suffer more
severely from distribution shift.
###
8.7 Feedback loops
Finally, we have restricted our attention to settings where the data distribution is independent of the model. When the data distribution does depend on the model, distribution shifts can arise from feedback loops between the data and the model. Examples include recommendation systems and other consumer products (Bottou et al., [2013](#bib.bib56); Hashimoto et al., [2018](#bib.bib166)); dialogue agents (Li et al., [2017b](#bib.bib234));
molecular compound optimization (Cuccarese et al., [2020](#bib.bib99); Reker, [2020](#bib.bib311));
decision systems (Liu et al., [2018](#bib.bib242); D’Amour et al., [2020b](#bib.bib103)); and adversarial settings like fraud or malware detection (Rigaki and Garcia, [2018](#bib.bib316)).
While these adaptive settings are outside the scope of our benchmark,
dealing with these types of distribution shifts is an important area of ongoing work.
9 Guidelines for method developers
-----------------------------------
We now discuss some community guidelines for method development using Wilds.
More specific submission guidelines for our leaderboard can be found at
<https://wilds.stanford.edu>.
###
9.1 General-purpose and specialized training algorithms
Wilds is primarily designed as a benchmark for developing and evaluating algorithms for training models that are robust to distribution shifts.
To facilitate systematic comparisons of these algorithms,
we encourage algorithm developers to use the standardized datasets (i.e., with no external data) and default model architectures provided in Wilds,
as doing so will help to isolate the contributions of the algorithm versus the training dataset or model architecture.
Our primary leaderboard will focus on submissions that follow these guidelines.
Moreover, we encourage developers to test their algorithms on all applicable Wilds datasets, so as to assess how well they do across different types of data and distribution shifts. We emphasize that it is still an open question
if a single general-purpose training algorithm can produce models that do well on all of the datasets without accounting for the particular structure of the distribution shift in each dataset.
As such, it would still be a substantial advance if an algorithm significantly improves performance on one type of shift but not others;
we aim for Wilds to facilitate research into both general-purpose algorithms as well as ones that are more specifically tailored to a particular application and type of distribution shift.
###
9.2 Methods beyond training algorithms
Beyond new training algorithms, there are many other promising directions for improving distributional robustness, including new model architectures and pre-training on additional external data beyond what is used in our default models. We encourage developers to test these approaches on Wilds as well, and we will track all such submissions on a separate leaderboard from the training algorithm leaderboard.
###
9.3 Avoiding overfitting to the test distribution
While each Wilds dataset aims to benchmark robustness to a type of distribution shift (e.g., shifts to unseen hospitals), practical limitations mean that for some datasets, we have data from only a limited number of domains (e.g., one OOD test hospital in Camelyon17-wilds).
As there can be substantial variability in performance across domains,
developers should be careful to avoid overfitting to the specific test sets in Wilds, especially on datasets like Camelyon17-wilds with limited test domains.
We strongly encourage all model developers to use the provided OOD validation sets for development and model selection, and to only use the OOD test sets for their final evaluations.
###
9.4 Reporting both ID and OOD performance
Prior work has shown that for many tasks, ID and OOD performance can be highly correlated across different model architectures and hyperparameters (Taori et al., [2020](#bib.bib365); Liu et al., [2021b](#bib.bib243); Miller et al., [2021](#bib.bib265)).
It is reasonable to expect that methods for improving ID performance could also give corresponding improvements in OOD performance in Wilds, and we welcome submissions of such methods.
To better understand the extent to which any gains in OOD performance can be attributed to improved ID performance versus a model that is more robust to (i.e., less affected by) the distribution shift,
we encourage model developers to report both ID and OOD performance numbers.
See Miller et al. ([2021](#bib.bib265)) for an in-depth discussion of this point.
###
9.5 Extensions to other problem settings
In this paper, we focused on the domain generalization and subpopulation shift settings.
In Appendix [C](#S3a "C Potential extensions to other problem settings ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we discuss how Wilds can be used in other realistic problem settings that allow training algorithms to leverage additional information, such as unlabeled test data in unsupervised domain adaptation (Ben-David et al., [2006](#bib.bib43)).
These sources of leverage could be fruitful approaches to improving OOD performance, and we welcome community contributions towards this effort.
10 Using the Wilds package
---------------------------
Finally, we discuss our open-source PyTorch-based package that exposes a simple interface to our datasets and automatically handles data downloads, allowing users to get started on a Wilds dataset in just a few lines of code.
In addition, the package provides various data loaders and utilities surrounding domain annotations and other metadata, which supports training algorithms that need access to these metadata.
The package also provides standardized evaluations for each dataset.
More documentation and installation information can be found at <https://wilds.stanford.edu>.
##### Datasets and data loading.
The Wilds package provides a simple, standardized interface for all datasets in the benchmark as well as their data loaders, as summarized in Figure [13](#S10.F13 "Figure 13 ‣ Datasets and data loading. ‣ 10 Using the Wilds package ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
This short code snippet covers all of the steps of getting started with a Wilds dataset, including dataset download and initialization, accessing various splits, and initializing the data loader.
We also provide multiple data loaders in order to accommodate a wide array of algorithms, which often require specific data loading schemes.
Figure 13:
Dataset initialization and data loading.
##### Domain information.
To allow algorithms to leverage domain annotations as well as other groupings over the available metadata, the Wilds package provides Grouper objects.
Grouper objects (e.g., grouper in Figure [14](#S10.F14 "Figure 14 ‣ Domain information. ‣ 10 Using the Wilds package ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")) extract group annotations from metadata, allowing users to specify the grouping scheme in a flexible fashion.
Figure 14:
Accessing domain and other group information via a Grouper object.
##### Evaluation.
Finally, the Wilds package standardizes and automates the evaluation for each dataset.
As summarized in Figure [15](#S10.F15 "Figure 15 ‣ Evaluation. ‣ 10 Using the Wilds package ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), invoking the eval method of each dataset yields all metrics reported in the paper and on the leaderboard.
Figure 15:
Evaluation.
Reproducibility
---------------
An executable version of our paper, hosted on CodaLab, can be found at <https://wilds.stanford.edu/codalab>. This contains the exact commands, code, environment, and data used for the experiments reported in our paper, as well as all trained model weights. The WILDS package is open-source and can be found at <https://github.com/p-lambda/wilds>.
Acknowledgements
----------------
Many people generously volunteered their time and expertise to advise us on Wilds.
We are grateful for all of the helpful suggestions and constructive feedback from:
Aditya Khosla,
Andreas Schlueter,
Annie Chen,
Aleksander Madry,
Alexander D’Amour,
Allison Koenecke,
Alyssa Lees,
Ananya Kumar,
Andrew Beck,
Behzad Haghgoo,
Charles Sutton,
Christopher Yeh,
Cody Coleman,
Dan Hendrycks,
Dan Jurafsky,
Daniel Levy,
Daphne Koller,
David Tellez,
Erik Jones,
Evan Liu,
Fisher Yu,
Georgi Marinov,
Hongseok Namkoong,
Irene Chen,
Jacky Kang,
Jacob Schreiber,
Jacob Steinhardt,
Jared Dunnmon,
Jean Feng,
Jeffrey Sorensen,
Jianmo Ni,
John Hewitt,
John Miller,
Kate Saenko,
Kelly Cochran,
Kensen Shi,
Kyle Loh,
Li Jiang,
Lucy Vasserman,
Ludwig Schmidt,
Luke Oakden-Rayner,
Marco Tulio Ribeiro,
Matthew Lungren,
Megha Srivastava,
Nelson Liu,
Nimit Sohoni,
Pranav Rajpurkar,
Robin Jia,
Rohan Taori,
Sarah Bird,
Sharad Goel,
Sherrie Wang,
Shyamal Buch,
Stefano Ermon,
Steve Yadlowsky,
Tatsunori Hashimoto,
Tengyu Ma,
Vincent Hellendoorn,
Yair Carmon,
Zachary Lipton,
and Zhenghao Chen.
The design of the WILDS benchmark was inspired by the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)), and we are grateful to the Open Graph Benchmark team for their advice and help in setting up our benchmark.
This project was funded by an Open Philanthropy Project Award and NSF Award Grant No. 1805310.
Shiori Sagawa was supported by the Herbert Kunzel Stanford Graduate Fellowship.
Henrik Marklund was supported by the Dr. Tech. Marcus Wallenberg Foundation for Education in International Industrial Entrepreneurship, CIFAR, and Google.
Sang Michael Xie and Marvin Zhang were supported by NDSEG Graduate Fellowships.
Weihua Hu was supported by the Funai Overseas Scholarship and the Masason Foundation Fellowship.
Sara Beery was supported by an NSF Graduate Research Fellowship and is a PIMCO Fellow in Data Science.
Jure Leskovec is a Chan Zuckerberg Biohub investigator.
Chelsea Finn is a CIFAR Fellow in the Learning in Machines and Brains Program.
We also gratefully acknowledge the support of DARPA under Nos. N660011924033 (MCS);
ARO under Nos. W911NF-16-1-0342 (MURI), W911NF-16-1-0171 (DURIP);
NSF under Nos. OAC-1835598 (CINES), OAC-1934578 (HDR), CCF-1918940 (Expeditions), IIS-2030477 (RAPID); Stanford Data Science Initiative, Wu Tsai Neurosciences Institute, Chan Zuckerberg Biohub, Amazon, JPMorgan Chase, Docomo, Hitachi, JD.com, KDDI, NVIDIA, Dell, Toshiba, and UnitedHealth Group.
A Dataset realism
------------------
In this section, we discuss the framework we use to assess the realism of a benchmark dataset.
Realism is subtle to pin down and highly contextual, and assessing realism often requires consulting with domain experts and practitioners. As a general framework, we can view a benchmark dataset as comprising the data, a task and associated evaluation metric, and a train/test split that potentially reflects a distribution shift.
Each of these components can independently be more or less realistic:
1. 1.
The data—which includes not just the inputs x𝑥xitalic\_x but also any associated metadata (e.g., the domain that each data point came from)— is realistic if it accurately reflects what would plausibly be collected and available for a model to use in a real application.
The realism of data also depends on the application context; for example, using medical images captured with state-of-the-art equipment might be realistic for well-equipped hospitals, but not necessarily for clinics that use older generations of the technology, or vice versa.
Extreme examples of unrealistic data include the Gaussian distributions that are often used to cleanly illustrate the theoretical properties of various algorithms.
2. 2.
The task and evaluation metric is realistic if the task is relevant to a real application and if the metric measures how successful a model would be in that application.
Here and with the other components, realism lies on a spectrum.
For example, in a wildlife conservation application where the inputs are images from camera traps, the real task might be to estimate species populations (Parham et al., [2017](#bib.bib285)), i.e., the number of distinct individual animals of each species seen in the overall collection of images; a task that is less realistic but still relevant and useful for ecologists might be to classify what species of animal is seen in each image (Tabak et al., [2019](#bib.bib363)).
The choice of evaluation metric is also important. In the wildlife example, conservationists might care more about rare species than common species, so measuring average classification accuracy would be less realistic than a metric that prioritizes classifying the rare species correctly.
3. 3.
The distribution shift (train/test split) is realistic if it reflects training and test distributions that might arise in deployment for that dataset and task.
For example, if a medical algorithm is trained on data from a few hospitals and then expected to be deployed more widely, then it would be realistic to test it on hospitals that are not in the training set.
On the other hand, an example of a less realistic shift is to, for instance, train a pedestrian classifier entirely on daytime photos and then test it only on nighttime photos;
in practice, any reasonable dataset for pedestrian detection that is used in a real application would include both daytime and nighttime photos.
Through the lens of this framework, existing ML benchmarks tend to focus on object recognition tasks with realistic data (e.g., photos) but not necessarily with realistic distribution shifts.
With Wilds, we seek to address this gap by selecting datasets that represent a wide variety of tasks (with realistic evaluation metrics and data) and that reflect realistic distribution shifts, i.e., train/test splits that are likely to arise in real-world deployments.
To elaborate on the realism of the distribution shift, we associate each dataset in Wilds with the distribution shift (i.e., problem setting) that we believe best reflects the real-world challenges in the corresponding application area.
For example, domain generalization is a realistic setting for the Camelyon17-wilds dataset as medical models are typically trained on data collected from a handful of hospitals, but with the goal of general deployment across different hospitals.
On the other hand, subpopulation shift is appropriate for the CivilComments-wilds dataset, as the real-world challenge is that some demographic subpopulations (domains) are underrepresented, rather than completely unseen, in the training data.
The appropriate problem setting depends on many dataset-specific factors, but some common considerations include:
* •
Domain type. Certain types of domains are generally more appropriate for a particular setting. For example, if the domains represent time, as in FMoW-wilds, then domain generalization is suitable as a common challenge is to generalize from past data to future data.
On the other hand, if the domains represent demographics and the goal is to improve performance on minority subpopulations, as in CivilComments-wilds, then subpopulation shift is typically more appropriate.
* •
Data collection challenges. When collecting data from a new domain is expensive, domain generalization is often appropriate, as we might want to train on data from a limited number of domains but still generalize to unseen domains. For example, it is difficult to collect patient data from multiple hospitals, as in Camelyon17-wilds, or survey data from new countries, as in PovertyMap-wilds.
* •
Continuous addition of new domains. A special case of the above is when new domains are continuously created. For example, in Amazon-wilds, where domains correspond to users, new users are constantly signing up for the platform; and in iWildCam2020-wilds, where domains correspond to camera traps, new cameras are constantly being deployed. These are natural domain generalization settings.
B Prior work on ML benchmarks for distribution shifts
------------------------------------------------------
In this section, we discuss existing ML distribution shift benchmarks in more detail, categorizing them by how they induce their respective distribution shifts.
We focus here on work that has appeared in ML conferences and journals; we discuss related work from other research communities in Section [8](#S8 "8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and Appendix [E](#S5a "E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
We also restrict our attention to publicly-available datasets.
While others have studied some proprietary datasets with realistic distribution shifts, such as the StreetView StoreFronts dataset (Hendrycks et al., [2020b](#bib.bib175)) or diabetic retinopathy datasets (D’Amour et al., [2020a](#bib.bib102)), these datasets are not publicly available due to privacy and other commercial reasons.
##### Distribution shifts from transformations.
Some of the most widely-adopted benchmarks induce distribution shifts by synthetically transforming the data.
Examples include rotated and translated versions of MNIST and CIFAR (Worrall et al., [2017](#bib.bib408); Gulrajani and Lopez-Paz, [2020](#bib.bib158));
surface variations such as texture, color, and corruptions like blur in Colored MNIST (Gulrajani and Lopez-Paz, [2020](#bib.bib158)), Stylized ImageNet (Geirhos et al., [2018a](#bib.bib142)), ImageNet-C (Hendrycks and Dietterich, [2019](#bib.bib172)),
and similar ImageNet variants (Geirhos et al., [2018b](#bib.bib143));
and datasets that crop out objects and replace their backgrounds, as in the Backgrounds Challenge (Xiao et al., [2020](#bib.bib414)) and other similar datasets (Sagawa et al., [2020a](#bib.bib327); Koh et al., [2020](#bib.bib209)).
Benchmarks for adversarial robustness also fall in this category of distribution shifts from transformations (Goodfellow et al., [2015](#bib.bib153); Croce et al., [2020](#bib.bib97)).
Though adversarial robustness is not a focus of this work,
we note that recent work on temporal perturbations with the ImageNet-Vid-Robust and YTBB-Robust datasets (Shankar et al., [2019](#bib.bib337))
represents a different form of distribution shift that also impacts real-world applications.
Outside of visual object recognition, other work has used synthetic datasets and transformations to explore compositional generalization, e.g., SCAN (Lake and Baroni, [2018](#bib.bib218)).
We discuss this more in Section [8](#S8 "8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
##### Synthetic-to-real transfers.
Fully synthetic datasets such as SYNTHIA (Ros et al., [2016](#bib.bib321)) and StreetHazards (Hendrycks et al., [2020a](#bib.bib174)) have been adopted for out-of-distribution detection as well as domain adaptation and generalization, e.g., by testing robustness to transformations in the seasons, weather, time, or architectural style (Hoffman et al., [2018](#bib.bib178); Volpi et al., [2018](#bib.bib389)).
While the data is synthetic, it can still look realistic if a high-fidelity simulator is used.
In particular, synthetic benchmarks that study transfers from synthetic to real data (Ganin and Lempitsky, [2015](#bib.bib136); Richter et al., [2016](#bib.bib315); Peng et al., [2018](#bib.bib289)) can be important tools for tackling real-world problems: even though the data is synthesized and by definition, not real, the synthetic-to-real distribution shift can still be realistic in contexts where real data is much harder to acquire than synthetic data (Bellemare et al., [2020](#bib.bib42)).
In this work, we do not study these types of synthetic distribution shifts; instead, we focus on distribution shifts that occur in the wild between real data distributions.
##### Distribution shifts from constrained splits.
Other benchmarks do not rely on transformations but instead split the data in a way that induces particular distribution shifts.
These benchmarks have realistic data, e.g., the data points are derived from real-world photos,
but they do not necessarily reflect distribution shifts that would arise in the wild.
For example, BREEDS (Santurkar et al., [2020](#bib.bib331)) and a related dataset (Hendrycks and Dietterich, [2019](#bib.bib172)) test generalization to unseen ImageNet subclasses by holding out subclasses specified by several controllable parameters;
similarly, NICO (He et al., [2020](#bib.bib168)) considers subclasses that are defined by their context, such as dogs at home versus dogs on the beach;
DeepFashion-Remixed (Hendrycks et al., [2020b](#bib.bib175)) constrains the training set to include only photos from a single camera viewpoint and tests generalization to unseen camera viewpoints;
BDD-Anomaly (Hendrycks et al., [2020a](#bib.bib174)) uses a driving dataset but with all motorcycles, trains, and bicycles removed from the training set only;
and ObjectNet (Barbu et al., [2019](#bib.bib29)) comprises images taken from a few pre-specified viewpoints, allowing for systematic evaluation for robustness to camera angle changes but deviating from natural camera angles.
##### Distribution shifts across datasets.
A well-studied special case of the above category is the class of distribution shifts obtained by combining several disparate datasets (Torralba and Efros, [2011](#bib.bib377)), training on one or more of them and then testing on the remaining datasets.
A recent influential example is the ImageNetV2 dataset (Recht et al., [2019](#bib.bib308)), which was constructed to be similar to the original ImageNet dataset.
Unlike ImageNetV2, however, many of these distribution shifts were constructed to be more drastic than might arise in the wild.
For example, standard domain adaptation benchmarks include training on MNIST but testing on SVHN street signs (LeCun et al., [1998](#bib.bib226); Yuval et al., [2011](#bib.bib425); Tzeng et al., [2017](#bib.bib379); Hoffman et al., [2018](#bib.bib178)),
as well as transfers across datasets containing different renditions (e.g., photos, clipart, sketches) in DomainNet (Peng et al., [2019](#bib.bib290)) and the Office-Home dataset (Venkateswara et al., [2017](#bib.bib386)).
The main difference between domain adaptation and domain generalization is that in the latter, we do not assume access to unlabeled data from the test distribution.
This makes it straightforward to use domain adaptation benchmarks for domain generalization, e.g., in DomainBed (Gulrajani and Lopez-Paz, [2020](#bib.bib158)); we focus on domain generalization in this work,
but further discuss unsupervised domain adaptation in Section [C](#S3a "C Potential extensions to other problem settings ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Other similar benchmarks that have been proposed for domain generalization include VLCS (Fang et al., [2013](#bib.bib128)), which tests generalization across similar visual object recognition datasets; PACS (Li et al., [2017a](#bib.bib229)), which (like DomainNet) tests generalization across datasets with different renditions; and ImageNet-R (Hendrycks et al., [2020b](#bib.bib175)) and ImageNet-Sketch (Wang et al., [2019c](#bib.bib393)), which also test generalization across different renditions by collecting separate datasets from Flickr and Google Image queries.
C Potential extensions to other problem settings
-------------------------------------------------
In this paper, we have focused on two problem settings involving domain shifts: domain generalization and subpopulation shifts.
Here, we discuss other problem settings within the framework of domain shifts that could also apply to Wilds datasets.
Using Wilds to benchmark and develop algorithms for these settings is an important avenue for future work, and we welcome community contributions towards this effort.
###
C.1 Problem settings in domain shifts
Within the general framework of domain shifts, specific problem settings can differ along the following axes of variation:
1. 1.
Seen versus unseen test domains.
Test domains may be seen during training time (𝒟𝗍𝖾𝗌𝗍⊆𝒟𝗍𝗋𝖺𝗂𝗇superscript𝒟𝗍𝖾𝗌𝗍superscript𝒟𝗍𝗋𝖺𝗂𝗇\mathcal{D}^{\mathsf{test}}\subseteq\mathcal{D}^{\mathsf{train}}caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT ⊆ caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT), as in subpopulation shift, or unseen
(𝒟𝗍𝗋𝖺𝗂𝗇∩𝒟𝗍𝖾𝗌𝗍=∅superscript𝒟𝗍𝗋𝖺𝗂𝗇superscript𝒟𝗍𝖾𝗌𝗍\mathcal{D}^{\mathsf{train}}\cap\mathcal{D}^{\mathsf{test}}=\emptysetcaligraphic\_D start\_POSTSUPERSCRIPT sansserif\_train end\_POSTSUPERSCRIPT ∩ caligraphic\_D start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT = ∅), as in domain generalization.
The domain generalization and subpopulation shift settings mainly differ on this factor.
2. 2.
Train-time domain annotations.
The domain identity d𝑑ditalic\_d may be observed for none, some, or all of the training examples.
Train-time domain annotations are straightforward to obtain in some settings, e.g., we should know which patients in the training sets came from which hospitals, but can be harder to obtain in some settings, e.g., we might only have demographic information on a subset of training users. In our domain generalization and subpopulation shift settings, d𝑑ditalic\_d is always observed at training time.
3. 3.
Test-time domain annotations.
The domain identity d𝑑ditalic\_d may be observed for none, some, or all of the test examples.
Test-time domain annotations allow models to be domain-specific, e.g., by treating domain identity as a feature if the train and test domains overlap.
For example, if the domains correspond to continents and the data to satellite images from a continent, we would presumably know what continent each image was taken from.
On the other hand, if the domains correspond to demographic information, this might be hard to obtain at test time (as well as training time, as mentioned above).
In domain generalization, d𝑑ditalic\_d may be observed at test time, but it is not helpful by itself as all of the test domains are unseen at training time. However, when combined with test-time unlabeled data, observing the domain d𝑑ditalic\_d at test time could help with adaptation.
In subpopulation shift, we typically assume that d𝑑ditalic\_d is unobserved at test time, though this need not always be true.
4. 4.
Test-time unlabeled data.
Varying amounts of unlabeled test data—samples of x𝑥xitalic\_x drawn from the test distribution P𝗍𝖾𝗌𝗍superscript𝑃𝗍𝖾𝗌𝗍P^{\mathsf{test}}italic\_P start\_POSTSUPERSCRIPT sansserif\_test end\_POSTSUPERSCRIPT—may be available, from none to a small batch to a large pool. This affects the degree to which models can adapt to test distributions.
For example, if the domains correspond to locations and the data points to photos taken at those locations, we might assume access to some unlabeled photos taken at the test locations.
Each combination of the above four factors corresponds to a specific problem setting with a different set of applicable methods.
In the current version of the Wilds benchmark, we focus on domain generalization and subpopulation shifts, which represent specific configurations of these factors.
We briefly discuss a few other problem settings in the remainder of this section.
###
C.2 Unsupervised domain adaptation
In the presence of distribution shift, a potential source of leverage is observing unlabeled test points from the test distribution.
In the unsupervised domain adaptation setting, we assume that at training time, we have access to a large amount of unlabeled data from each test distribution of interest, as well as the resources to train a separate model for each test distribution.
For example, in a satellite imagery setting like FMoW-wilds, it might be appropriate to assume that we have access to a large set of unlabeled recent satellite images from each continent and the wherewithal to train a separate model for each continent.
Many of the methods for domain generalization discussed in Section [6](#S6 "6 Baseline algorithms for distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") were originally methods for domain adaptation, since methods for both settings share the common goal of learning models that can transfer between domains. For example, methods that learn features that have similar distributions across domains are equally applicable to both settings
(Ben-David et al., [2006](#bib.bib43); Long et al., [2015](#bib.bib246); Sun et al., [2016](#bib.bib357); Ganin et al., [2016](#bib.bib137); Tzeng et al., [2017](#bib.bib379); Shen et al., [2018](#bib.bib339); Wu et al., [2019b](#bib.bib411)).
In fact, the CORAL algorithm that we use as a baseline in this work was originally developed for, and successfully applied in, unsupervised domain adaptation (Sun and Saenko, [2016](#bib.bib356)).
Other methods rely on knowing the test distribution and are thus specific to domain adaptation, e.g., learning to map data points from source to target domains (Hoffman et al., [2018](#bib.bib178)),
or estimating the test label distribution from unlabeled test data (Saerens et al., [2002](#bib.bib326); Zhang et al., [2013](#bib.bib428); Lipton et al., [2018](#bib.bib240); Azizzadenesheli et al., [2019](#bib.bib23); Alexandari et al., [2020](#bib.bib8); Garg et al., [2020](#bib.bib138)).
###
C.3 Test-time adaptation
A closely related setting to unsupervised domain adaptation is test-time adaptation, which also assumes the availability of unlabeled test data.
For datasets where there are many potential test domains (e.g., in iWildCam2020-wilds, we want a model that can ideally generalize to any camera trap), it might be infeasible to train a separate model for each test domain, as unsupervised domain adaptation would require.
In the test-time adaptation setting, we assume that a model is allowed to adapt to a small amount of unlabeled test data in a way that is computationally much less intensive than typical domain adaptation methods.
This is a difference of degree and not of kind, but it can have significant practical implications. For example, domain adaptation approaches typically require access to the training set and a large unlabeled test set at the same time, whereas test-time adaptation methods typically only require the learned model (which can be much smaller than the original training set) as well as a smaller amount of unlabeled test data.
A number of test-time adaptation methods have been recently proposed
(Li et al., [2017c](#bib.bib236); Sun et al., [2020b](#bib.bib359); Wang et al., [2020a](#bib.bib392)).
For example, adaptive risk minimization (ARM) is a meta-learning approach that adapts models to each batch of test examples under the assumption that all data points in a batch come from the same domain (Zhang et al., [2020](#bib.bib429)).
Many datasets in Wilds are suitable for the test-time adaptation setting.
For example, in iWildCam2020-wilds, images from the same domain are highly similar, sharing the same location, background, and camera angle, and prior work has shown inferring these shared features can improve performance considerably (Beery et al., [2020b](#bib.bib39)).
###
C.4 Selective prediction
A different problem setting that is orthogonal to the settings described above is selective prediction.
In the selective prediction setting, models are allowed to abstain on points where their confidence is below a certain threshold.
This is appropriate when, for example, abstentions can be handled by backing off to human experts, such as pathologists for Camelyon17-wilds, content moderators for CivilComments-wilds, wildlife experts for iWildCam2020-wilds, etc.
Many methods for selective prediction have been developed, from simply using softmax probabilities as a proxy for confidence (Cordella et al., [1995](#bib.bib95); Geifman and El-Yaniv, [2017](#bib.bib139)),
to methods involving ensembles of models (Gal and Ghahramani, [2016](#bib.bib135); Lakshminarayanan et al., [2017](#bib.bib219); Geifman et al., [2018](#bib.bib141))
or jointly learning to abstain and classify (Bartlett and Wegkamp, [2008](#bib.bib30); Geifman and El-Yaniv, [2019](#bib.bib140); Feng et al., [2019](#bib.bib129)).
Intuitively, even if a model is not robust to a distribution shift,
it might at least be able to maintain high accuracies on some subset of points that are close to the training distribution, while abstaining on the other points.
Indeed, prior work has shown that selective prediction can improve model accuracy under distribution shifts
(Pimentel et al., [2014](#bib.bib297); Hendrycks and Gimpel, [2017](#bib.bib173); Liang et al., [2018](#bib.bib238); Ovadia et al., [2019](#bib.bib283); Feng et al., [2019](#bib.bib129); Kamath et al., [2020](#bib.bib198)).
However, distribution shifts still pose a problem for selective prediction methods;
for instance, it is difficult to maintain desired abstention rates under distribution shifts (Kompa et al., [2020](#bib.bib210)), and confidence estimates have been found to drift over time (e.g., Davis et al. ([2017](#bib.bib106))).
D Additional experimental details
----------------------------------
###
D.1 Model hyperparameters
For each hyperparameter setting, we used early stopping to pick the epoch with the best OOD validation performance (as measured by the specified metrics for each dataset described in Section [4](#S4 "4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), and then picked the model hyperparameters with the best early-stopped validation performance.
We found that this gave similar or slightly better OOD test performance than selecting hyperparameters using the ID validation set (Table [3](#S4.T3 "Table 3 ‣ D.1 Model hyperparameters ‣ D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
Using the OOD validation set for early stopping means that even if the training procedure does not explicitly use additional metadata, as in ERM, the metadata might still be implicitly (but mildly) used for model selection in one of two related ways. First, the metric might use the metadata directly (e.g., by computing the accuracy over different subpopulations defined in the metadata). Second, the OOD validation set is generally selected according to this metadata (e.g., comprising data from a disjoint set of domains as the training set).
We expect that implicitly using the metadata in these ways should increase the OOD performance of each model. Nevertheless, as Sections [5](#S5 "5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and [6](#S6 "6 Baseline algorithms for distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") show, there are still large gaps between OOD and ID performance.
In general, we selected model hyperparameters with ERM and used the same hyperparameters for the other algorithm baselines (e.g., CORAL, IRM, or Group DRO).
For CORAL and IRM, we did a subsequent grid search over the weight of the penalty term,
using the defaults from Gulrajani and Lopez-Paz ([2020](#bib.bib158)). Specifically, we tried penalty weights of {0.1,1,10}0.1110\{0.1,1,10\}{ 0.1 , 1 , 10 } for CORAL and penalty weights of {1,10,100,1000}1101001000\{1,10,100,1000\}{ 1 , 10 , 100 , 1000 } for IRM.
We fixed the step size hyperparameter for Group DRO to its default value of 0.01 (Sagawa et al., [2020a](#bib.bib327)).
Table 3: The performance of models trained with empirical risk minimization with hyperparameters tuned using the out-of-distribution (OOD) vs. in-distribution (ID) validation set.
We excluded OGB-MolPCBA, RxRx1-wilds, and GlobalWheat-wilds, as they do not have separate ID validation sets, and CivilComments-wilds, which is a subpopulation shift setting where we measure worst-group accuracy on a validation set that is already identically distributed to the training set.
| | | | |
| --- | --- | --- | --- |
| | | ID performance | OOD performance |
| Dataset | Metric | Tuned on ID val | Tuned on OOD val | Tuned on ID val | Tuned on OOD val |
| iWildCam2020-wilds | Macro F1 | 47.2 (2.0) | 47.0 (1.4) | 29.8 (0.6) | 31.0 (1.3) |
| Camelyon17-wilds | Average acc | 98.7 (0.1) | 93.2 (5.2) | 65.8 (4.9) | 70.3 (6.4) |
| FMoW-wilds | Worst-region acc | 58.0 (0.5) | 57.4 (0.2) | 31.9 (0.8) | 32.8 (0.5) |
| PovertyMap-wilds | Worst-U/R Pearson R | 0.65 (0.03) | 0.62 (0.04) | 0.46 (0.06) | 0.46 (0.07) |
| Amazon-wilds | 10th percentile acc | 72.0 (0.0) | 71.9 (0.1) | 53.8 (0.8) | 53.8 (0.8) |
| Py150-wilds | Method/class acc | 75.6 (0.0) | 75.4 (0.4) | 67.9 (0.1) | 67.9 (0.1) |
###
D.2 Replicates
We typically use a fixed train/validation/test split and report results averaged across 3 replicates (random seeds for model initialization and minibatch order), as well as the unbiased standard deviation over those replicates.
There are three exceptions to this.
For PovertyMap-wilds, we report results averaged over 5-fold cross validation, as model training is relatively fast on this dataset. For Camelyon17-wilds, results vary substantially between replicates, so we report results averaged over 10 replicates instead. Similarly, for CivilComments-wilds, we report results averaged over 5 replicates.
###
D.3 Baseline algorithms
For all classification datasets, we train models against the cross-entropy loss. For the PovertyMap-wilds regression dataset, we use the mean-squared-error loss.
We adapted the implementations of CORAL from Gulrajani and Lopez-Paz ([2020](#bib.bib158));
IRM from Arjovsky et al. ([2019](#bib.bib16)); and Group DRO from Sagawa et al. ([2020a](#bib.bib327)).
We note that CORAL was originally proposed in the context of domain adaptation (Sun and Saenko, [2016](#bib.bib356)), where it was shown to substantially improve performance on standard domain adaptation benchmarks, and it was subsequently adapted for domain generalization (Gulrajani and Lopez-Paz, [2020](#bib.bib158)).
Following these implementations, we use minibatch stochastic optimizers to train models under each algorithm, and we sample uniformly from each domain regardless of the number of training examples in it.
This means that the CORAL and IRM algorithms optimize for their respective penalty terms plus a reweighted ERM objective that weights each domain equally (i.e., effectively upweighting minority domains).
The Group DRO objective is unchanged, as it still optimizes for the domain with the worst loss, but the uniform sampling improves optimization stability.
Both CORAL and IRM are designed for models with featurizers, i.e., models that first map each input to a feature representation and then predict based on the representation.
To estimate the feature distribution for a domain, these algorithms need to see a sufficient number of examples from that domain in a minibatch.
However, some of our datasets have large numbers of domains, making it infeasible for each minibatch to contain examples from all domains.
For these algorithms, our data loaders form a minibatch by first sampling a few domains, and then sampling examples from those domains.
For consistency in our experiments, we used the same total batch size for these algorithms and for ERM and Group DRO, with a default of 8 examples per domain in each minibatch (e.g., if the batch size was 32, then in each minibatch we would have 8 examples ×\times× 4 domains).
For Group DRO, as in Sagawa et al. ([2020a](#bib.bib327)), each example in the minibatch is sampled independently with uniform probabilities across domains, and therefore each minibatch does not need to only comprise a small number of domains.
We note that reweighting methods like Group DRO are effective only when the training loss is non-vanishing, which we achieve through early stopping (Byrd and Lipton, [2019](#bib.bib69); Sagawa et al., [2020a](#bib.bib327), [b](#bib.bib328)).
E Additional dataset details and results
-----------------------------------------
In this section, we discuss each Wilds dataset in more detail. For completeness, we start by repeating the motivation behind each dataset from Section [4](#S4 "4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
We then describe the task, the distribution shift, and the evaluation criteria, and present baseline results that elaborate upon those in
Sections [5](#S5 "5 Performance drops from distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and [6](#S6 "6 Baseline algorithms for distribution shifts ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
We also discuss the broader context behind each dataset and how it connects with other distribution shifts in similar applications.
Finally, we describe how each dataset was modified from its original
version in terms of the evaluation, splits, and data.
Unless otherwise specified, all experiments follow the protocol laid out in Appendix [D](#S4a "D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
E.1 iWildCam2020-wilds
Animal populations have declined 68% on average since 1970 (Grooten et al., [2020](#bib.bib156)).
To better understand and monitor wildlife biodiversity loss, ecologists commonly deploy camera traps—heat or motion-activated static cameras placed in the wild (Wearn and Glover-Kapfer, [2017](#bib.bib397))—and then use ML models to process the data collected (Weinstein, [2018](#bib.bib399); Norouzzadeh et al., [2019](#bib.bib277); Tabak et al., [2019](#bib.bib363); Beery et al., [2019](#bib.bib38); Ahumada et al., [2020](#bib.bib5)).
Typically, these models would be trained on photos from some existing camera traps and then used across new camera trap deployments.
However, across different camera traps, there is drastic variation in illumination, color, camera angle, background, vegetation, and relative animal frequencies,
which results in models generalizing poorly to new camera trap deployments (Beery et al., [2018](#bib.bib36)).
We study this shift on a variant of the iWildCam 2020 dataset (Beery et al., [2020a](#bib.bib37)).
####
E.1.1 Setup
##### Problem setting.
We consider the domain generalization setting, where the domains are camera traps, and we seek to learn models that generalize to photos taken from new camera deployments (Figure [3](#S4.F3 "Figure 3 ‣ 4.1.1 iWildCam2020-wilds: Species classification across different camera traps ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The task is multi-class species classification.
Concretely, the input x𝑥xitalic\_x is a photo taken by a camera trap,
the label y𝑦yitalic\_y is one of 182 different animal species,
and the domain d𝑑ditalic\_d is an integer that identifies the camera trap that took the photo.
##### Data.
The dataset comprises 203,029 images from 323 different camera traps spread across multiple countries in different parts of the world. The original camera trap data comes from the Wildlife Conservation Society (<http://lila.science/datasets/wcscameratraps>).
These images tend to be taken in short bursts following motion-activation of a camera trap, so the images can be additionally grouped into sequences of images from the same burst, though our baseline models do not exploit this information and our evaluation metric treats each image individually.
Each image is associated with the following metadata: camera trap ID, sequence ID, and datetime.
As is typical for camera trap data, approximately 35% of the total number of images are empty (i.e., do not contain any animal species); this corresponds to one of the 182 class labels. The ten most common classes across the full dataset are “empty” (34%), ocellated turkey (8%), great curassow (6%), impala (4%), black-fronted duiker (4%), white-lipped peccary (3%), Central American agouti (3%), ocelot (3%), gray fox (2%) and cow (2%).
We note that the labels in this dataset can be somewhat noisy, as is typical of camera trap data. Some ecologists might label all images in a sequence as the same animal (which can result in empty/dark frames being labeled as an animal), whereas other ecologists might try to label it frame-by-frame. This label noise imposes a natural ceiling on model performance, though the label noise is equally present in ID vs. OOD data.
We split the dataset by randomly partitioning the data by camera traps:
1. 1.
Training: 129,809 images taken by 243 camera traps.
2. 2.
Validation (OOD): 14,961 images taken by 32 different camera traps.
3. 3.
Test (OOD): 42,791 images taken by 48 different camera traps.
4. 4.
Validation (ID): 7,314 images taken by the same camera traps as the training set, but on different days from the training and test (ID) images.
5. 5.
Test (ID): 8,154 images taken by the same camera traps as the training set, but on different days from the training and validation (ID) images.
The camera traps are randomly distributed across the training, validation (OOD), and test (OOD) sets. The number of examples per location vary widely from 1 to 8494, with a median of 194 images (Figure [16](#S5.F16 "Figure 16 ‣ Data. ‣ E.1.1 Setup ‣ E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
All images from the same sequence (i.e., all images taken in the same burst) are placed together in the same split. See Appendix [E.1.4](#S5.SS1.SSS4 "E.1.4 Additional details ‣ E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more details.
![Refer to caption]()
Figure 16: Number of examples per location in the iWildCam2020-wilds dataset. The locations are sorted such that locations with the least amount of examples are to the left on the x-axis.
##### Evaluation.
We evaluate models by their macro F1 score (i.e., we compute the F1 score for each class separately, then average those scores). We also report the average accuracy of each model across all test images, but primarily use the macro F1 score to better capture model performance on rare species. In the natural world, protected and endangered species are rare by definition, and are often the most important to accurately monitor. However, common species are much more likely to be captured in camera trap images; this imbalance can make metrics like average accuracy an inaccurate picture of model effectiveness.
##### Potential leverage.
Though the problem is challenging for existing ML algorithms, adapting to photos from different camera traps is simple and intuitive for humans. Repeated backgrounds and habitual animals, which cause each sensor to have a unique class distribution, provide a strong implicit signal across data from any one location.
We anticipate that approaches that utilize the provided camera trap annotations can learn to factor out these common features and avoid learning spurious correlations between particular backgrounds and animal species.
####
E.1.2 Baseline results
Figure 17: Label distribution for each iWildCam2020-wilds split.
##### Model.
For all experiments, we use ResNet-50 models (He et al., [2016](#bib.bib167)) that were pretrained on ImageNet,
using a learning rate of 3e-5 and no L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization.
As input, these models take in images resized to 448 by 448.
We trained these models with the Adam optimizer and a batch size of 16 for 12 epochs. To pick hyperparameters, we did a grid search over learning rates {1×10−5,3×10−5,1×10−4}1superscript1053superscript1051superscript104\{1\times 10^{-5},3\times 10^{-5},1\times 10^{-4}\}{ 1 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 3 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 1 × 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT } and L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT regularization strengths {0,1×10−3,1×10−2}01superscript1031superscript102\{0,1\times 10^{-3},1\times 10^{-2}\}{ 0 , 1 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT , 1 × 10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT }.
We report results aggregated over 3 random seeds.
##### ERM results and performance drops.
Model performance dropped substantially and consistently going from the train-to-train in-distribution (ID) setting to the official out-of-distribution (OOD) setting (Table [4](#S5.T4 "Table 4 ‣ Additional baseline methods. ‣ E.1.2 Baseline results ‣ E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")),
with a macro F1 score of 47.0 on the ID test set but only 31.0 on the OOD test set.
We note that macro F1 and average accuracy both differ between the OOD validation and test sets: this is in part due to the difference in class balance between them, which in turn is due to differences in the proportion of classes across camera traps.
In particular, macro F1 can vary between splits because we take the average F1 score across all classes that are present in the evaluation split, and not all splits have the same classes present (e.g., a rare species might be in the OOD validation set but not OOD test set, or vice versa). In additional, average accuracy can differ between splits due in part to variation in the fraction of empty images per location (e.g., the camera traps that were randomly assigned to the OOD validation set have a smaller proportion of empty images).
We only ran a train-to-train comparison because there are a relatively large number of domains (camera traps) split i.i.d. between the training and test sets, which suggests that the training and test sets should be “equally difficult”. The size of the ID-OOD gap in macro F1 is large enough that we expect it should hold up even in a test-to-test comparison.
However, the results in Table [4](#S5.T4 "Table 4 ‣ Additional baseline methods. ‣ E.1.2 Baseline results ‣ E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and Figure [17](#S5.F17 "Figure 17 ‣ E.1.2 Baseline results ‣ E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") show that there is substantial variability between domains, and it would be useful for future work to establish the magnitude of the ID-OOD gap under the test-to-test or mixed-to-test comparisons.
##### Additional baseline methods.
Table 4: Baseline results on iWildCam2020-wilds. In-distribution (ID) results correspond to the train-to-train setting. Parentheses show standard deviation across 3 replicates.
| | | | | |
| --- | --- | --- | --- | --- |
| | Val (ID) | Val (OOD) | Test (ID) | Test (OOD) |
| Algorithm | Macro F1 | Avg acc | Macro F1 | Avg acc | Macro F1 | Avg acc | Macro F1 | Avg acc |
| ERM | 48.8 (2.5) | 82.5 (0.8) | 37.4 (1.7) | 62.7 (2.4) | 47.0 (1.4) | 75.7 (0.3) | 31.0 (1.3) | 71.6 (2.5) |
| CORAL | 46.7 (2.8) | 81.8 (0.4) | 37.0 (1.2) | 60.3 (2.8) | 43.5 (3.5) | 73.7 (0.4) | 32.8 (0.1) | 73.3 (4.3) |
| IRM | 24.4 (8.4) | 66.9 (9.4) | 20.2 (7.6) | 47.2 (9.8) | 22.4 (7.7) | 59.9 (8.1) | 15.1 (4.9) | 59.8 (3.7) |
| Group DRO | 42.3 (2.1) | 79.3 (3.9) | 26.3 (0.2) | 60.0 (0.7) | 37.5 (1.7) | 71.6 (2.7) | 23.9 (2.1) | 72.7 (2.0) |
| Reweighted (label) | 42.5 (0.5) | 77.5 (1.6) | 30.9 (0.3) | 57.8 (2.8) | 42.2 (1.4) | 70.8 (1.5) | 26.2 (1.4) | 68.8 (1.6) |
We trained models with CORAL, IRM, and Group DRO, treating each camera trap as a domain, and using the same model hyperparameters as ERM.
These did not improve upon the ERM baseline (Table [4](#S5.T4 "Table 4 ‣ Additional baseline methods. ‣ E.1.2 Baseline results ‣ E.1 iWildCam2020-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The IRM models performed especially poorly on this dataset; we suspect that this is because the default estimator of the IRM penalty term can be negatively biased when examples are sampled without replacement from small domains, but further investigation is needed.
We also tried reweighting the training data so that each label had equal weight, but this did not improve over ERM either.
##### Discussion.
Across locations, there is drastic variation in illumination, camera angle, background, vegetation, and color. This variation, coupled with considerable differences in the distribution of animals between camera traps, likely encourages the model to overfit to specific animal species appearing in specific locations, which may account for the performance drop.
The original iWildCam 2020 competition allows users to use MegaDetector (Beery et al., [2019](#bib.bib38)), which is an animal detector trained on a large set of data beyond what is provided in the training set.
Using an animal detection model like MegaDetector typically improves classification performance on camera traps (Beery et al., [2018](#bib.bib36)).
However, we intentionally do not use MegaDetector in our baselines for iWildCam2020-wilds for two reasons.
First, though the trained MegaDetector model is publicly available, the MegaDetector training set is not, which makes it difficult to build on top of it and run controlled experiments.
Second, bounding box annotations are costly and harder to obtain, and there is much more data with image-level species label, so it would be useful to be able to train models that do not have to rely on bounding box annotations.
We still welcome leaderboard submissions that use MegaDetector, as it is useful to see how much better models can perform when they use MegaDetector or other similar animal detectors, but we will distinguish these submissions from others that only use what is provided in the training set.
A different source of leverage comes from the temporal signal in the camera trap images, which are organized into sequences that each correspond to a burst of images from a single motion trigger.
Using this sequence information (e.g., by taking the median prediction across a sequence) can also improve model performance (Beery et al., [2018](#bib.bib36)),
and we welcome submissions that explore this direction.
####
E.1.3 Broader context
Differences across data distributions at different sensor locations is a common challenge in automated wildlife monitoring applications, including using audio sensors to monitor animals that are easier heard than seen such as primates, birds, and marine mammals (Crunchant et al., [2020](#bib.bib98); Stowell et al., [2019](#bib.bib354); Shiu et al., [2020](#bib.bib345)), and using static sonar to count fish underwater to help maintain sustainable fishing industries (Pipal et al., [2012](#bib.bib298); Vatnehol et al., [2018](#bib.bib384); Schneider and Zhuang, [2020](#bib.bib333)).
As with camera traps, each static audio sensor has a specific species distribution as well as a sensor specific background noise signature, making generalization to new sensors challenging. Similarly, static sonar used to measure fish escapement have sensor-specific background reflectance based on the shape of the river bottom.
Moreover, since species are distributed in a non-uniform and long-tailed fashion across the globe, it is incredibly challenging to collect sufficient samples for rare species to escape the low-data regime.
Implicitly representing camera-specific distributions and background features in per-camera memory banks and extracting relevant information from these via attention has been shown to help overcome some of these challenges for static cameras (Beery et al., [2020b](#bib.bib39)).
More broadly, shifts in background, image illumination and viewpoint have been studied in computer vision research. First, several works have shown that object classifiers often rely on the background rather than the object to make its classification (Rosenfeld et al., [2018](#bib.bib322); Shetty et al., [2019](#bib.bib341); Xiao et al., [2020](#bib.bib414)). Second, common perturbations such as blurriness or shifts in illumination, tend to reduce performance (Dodge and Karam, [2017](#bib.bib114); Temel et al., [2018](#bib.bib371); Hendrycks and Dietterich, [2019](#bib.bib172)).
Finally, shifts in rotation and viewpoint of the object has been shown to degrade performance (Barbu et al., [2019](#bib.bib29)).
####
E.1.4 Additional details
##### Data processing.
We generate the data splits in three steps. First, to generate the OOD splits, we randomly split all locations into three groups: Validation (OOD), Test (OOD), and Others. Then, to generate the train-to-train ID splits, we split the Others group uniformly by date at random into three sets: Training, Validation (ID), and Test (ID).
When doing the ID split, some locations only ended up in some of but not all of Training, Validation (ID), and Test (ID). For instance, if there were very few dates for a specific location (camera trap), it may be that no examples from that location ended up in the train split. This defeats the purpose of the ID split, which is to test performance on locations that were seen during training. We therefore put these locations in the train split. Finally, any images in the test set with classes not present in the train set were removed.
##### Modifications to the original dataset.
The original iWildCam 2020 Kaggle competition similarly split the dataset by camera trap, though the competition focused on average accuracy. We consider a smaller subset of the data here.
Specifically, the Kaggle competition uses a held-out test set that we are not utilizing, as the test set is intended to be reused in a future competition and is not yet public.
Instead, we constructed our own test set by splitting the Kaggle competition training data into our own splits: train, validation (ID), validation (OOD), test (ID), test (OOD).
Images are organized into sequences, but we treat each image separately. In the iWildCam 2020 competition, the top participants utilized the sequence data and also used a pretrained MegaDetector animal detection model that outputs bounding boxes over the animals. These images are cropped using the bounding boxes and then fed into a classification network. As we discuss above, we intentionally do not use MegaDetector in our experiments.
In addition, compared to the iWildCam 2020 competition, the iWildCam 2021 competition changed several class definitions (such as removing the “unknown” class) and removed some images that were taken indoors or had humans in the background. We have applied these updates to iWildCam2020-wilds as well.
###
E.2 Camelyon17-wilds
Models for medical applications are often trained on data from a small number of hospitals, but with the goal of being deployed more generally across other hospitals.
However, variations in data collection and processing can degrade model accuracy on data from new hospital deployments (Zech et al., [2018](#bib.bib427); AlBadawy et al., [2018](#bib.bib7)).
In histopathology applications—studying tissue slides under a microscope—this variation can arise from sources like differences in the patient population or in slide staining and image acquisition (Veta et al., [2016](#bib.bib387); Komura and Ishikawa, [2018](#bib.bib211); Tellez et al., [2019](#bib.bib370)).
We study this shift on a patch-based variant of the Camelyon17 dataset (Bandi et al., [2018](#bib.bib28)).
####
E.2.1 Setup
##### Problem setting.
We consider the domain generalization setting, where the domains are hospitals, and our goal is to learn models that generalize to data from a hospital that is not in the training set (Figure [4](#S4.F4 "Figure 4 ‣ 4.1.1 iWildCam2020-wilds: Species classification across different camera traps ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The task is to predict if a given region of tissue contains any tumor tissue,
which we model as binary classification.
Concretely, the input x𝑥xitalic\_x is a 96x96 histopathological image, the label y𝑦yitalic\_y is a binary indicator of whether the central 32x32 region contains any tumor tissue, and the domain d𝑑ditalic\_d is an integer that identifies the hospital that the patch was taken from.
##### Data.
The dataset comprises 450,000 patches extracted from 50 whole-slide images (WSIs) of breast cancer metastases in lymph node sections, with 10 WSIs from each of 5 hospitals in the Netherlands.
Each WSI was manually annotated with tumor regions by pathologists, and the resulting segmentation masks were used to determine the labels for each patch.
We also provide metadata on which slide (WSI) each patch was taken from, though our baseline algorithms do not use this metadata.
We split the dataset by domain (i.e., which hospital the patches were taken from):
1. 1.
Training: 302,436 patches taken from 30 WSIs, with 10 WSIs from each of the 3 hospitals in the training set.
2. 2.
Validation (OOD): 34,904 patches taken from 10 WSIs from the 4th hospital. These WSIs are distinct from those in the other splits.
3. 3.
Test (OOD): 85,054 patches taken from 10 WSIs from the 5th hospital, which was chosen because its patches were the most visually distinctive. These WSIs are also distinct from those in the other splits.
4. 4.
Validation (ID): 33,560 patches taken from the same 30 WSIs from the training hospitals.
We do not provide a Test (ID) set, as there is no practical setting in which we would have labels on a uniformly randomly sampled set of patches from a WSI, but no labels on the other patches from the same WSI.
##### Evaluation.
We evaluate models by their average test accuracy across patches. Histopathology datasets can be unwieldy for ML models, as individual images can be several gigabytes large; extracting patches involves many design choices; the classes are typically very unbalanced; and evaluation often relies on more complex slide-level measures such as the free-response receiver operating characteristic (FROC) (Gurcan et al., [2009](#bib.bib161)).
To improve accessibility, we pre-process the slides into patches and balance the dataset so that each split has a 50/50 class balance, making average accuracy is a reasonable measure of performance (Veeling et al., [2018](#bib.bib385); Tellez et al., [2019](#bib.bib370)).
##### Potential leverage.
Prior work has shown that differences in staining between hospitals are the primary source of variation in this dataset, and that specialized stain augmentation methods can close the in- and out-of-distribution accuracy gap on a variant of the dataset based on the same underlying slides (Tellez et al., [2019](#bib.bib370)).
However, the general task of learning histopathological models that are robust to variation across hospitals (from staining and other sources) is still an open research question.
In this way, the Camelyon17-wilds dataset is a controlled testbed for general-purpose methods that can learn to be robust to stain variation between hospitals, given a training set from multiple hospitals.
####
E.2.2 Baseline results
Table 5: Baseline results on Camelyon17-wilds. In-distribution (ID) results correspond to the train-to-train setting. Parentheses show standard deviation across 10 replicates. Note that the standard error of the mean is smaller (by a factor of 1010\sqrt{10}square-root start\_ARG 10 end\_ARG).
| | | | |
| --- | --- | --- | --- |
| Algorithm | Validation (ID) accuracy | Validation (OOD) accuracy | Test (OOD) accuracy |
| ERM | 93.2 (5.2) | 84.9 (3.1) | 70.3 (6.4) |
| CORAL | 95.4 (3.6) | 86.2 (1.4) | 59.5 (7.7) |
| IRM | 91.6 (7.7) | 86.2 (1.4) | 64.2 (8.1) |
| Group DRO | 93.7 (5.2) | 85.5 (2.2) | 68.4 (7.3) |
Table 6: Mixed-to-test comparison for ERM models on Camelyon17-wilds.
In the official OOD setting, we train on data from three hospitals and evaluate on a different test hospital, whereas in the mixed-to-test ID setting,
we add data from one extra slide from the test hospital to the training set.
The official Test (OOD) set has data from 10 slides, but for this comparison, we report performance for both splits on the same 9 slides (without the slide that was moved to the training set).
This makes the numbers (71.0 vs. 70.3) for the official split slightly different from Table [5](#S5.T5 "Table 5 ‣ E.2.2 Baseline results ‣ E.2 Camelyon17-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Parentheses show standard deviation across 10 replicates.
Note that the standard error of the mean is smaller (by a factor of 1010\sqrt{10}square-root start\_ARG 10 end\_ARG).
| | | |
| --- | --- | --- |
| Setting | Algorithm | Test (OOD) accuracy |
| Official (train on ID examples) | ERM | 71.0 (6.3) |
| Mixed-to-test (train on ID + OOD examples) | ERM | 82.9 (9.8) |
##### Model.
For all experiments, we use DenseNet-121 models (Huang et al., [2017](#bib.bib183)) models trained from scratch on the 96 ×\times× 96 patches, following prior work (Veeling et al., [2018](#bib.bib385)). These models used a learning rate of 10−3superscript10310^{-3}10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT, L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strength of 10−2superscript10210^{-2}10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT, a batch size of 32, and SGD with momentum (set to 0.9), trained for 5 epochs with early stopping.
We selected hyperparameters by a grid search over learning rates {10−4\{10^{-4}{ 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT, 10−3superscript10310^{-3}10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT, 10−2}10^{-2}\}10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT }, and L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strengths {0,10−3,10−2}0superscript103superscript102\{0,10^{-3},10^{-2}\}{ 0 , 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT }.
We report results aggregated over 10 random seeds.
##### ERM results and performance drops.
Table [5](#S5.T5 "Table 5 ‣ E.2.2 Baseline results ‣ E.2 Camelyon17-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that the model was consistently accurate on the train-to-train in-distribution (ID) validation set and to a lesser extent on the out-of-distribution (OOD) validation set, which was from a held-out hospital.
However, it was wildly inconsistent on the test set, which was from a different held-out hospital,
with a standard deviation of 6.4% in accuracies across 10 random seeds.
There is a large gap between train-to-train ID validation and OOD validation accuracy, and between OOD validation and OOD test accuracy (in part because we early stop on the highest OOD validation accuracy).
Nevertheless, we found that using the OOD validation set gave better results than using the ID validation set; see Appendix [D.1](#S4.SS1a "D.1 Model hyperparameters ‣ D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more discussion.
We ran an additional mixed-to-test comparison, where we moved 1 of the 10 slides777This slide was randomly chosen and corresponded to about 6% of the test patches; some slides contribute more patches than others because they contain larger tumor regions. from the test hospital to the training set and tested on the patches from the remaining 9 slides.
The mixed-to-test setting gives significantly higher accuracy on the reduced test set (Table [6](#S5.T6 "Table 6 ‣ E.2.2 Baseline results ‣ E.2 Camelyon17-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), suggesting that the observed performance drop is due to the distribution shift, as opposed to the intrinsic difficulty of the examples from the test hospital.
We note that this mixed-to-test comparison mixes in only a small amount of test data and is therefore likely to be an underestimate of in-distribution performance on the test set; we opted to only mix in 1 slide so as to preserve enough test examples to be able to accurately estimate model performance.
##### Additional baseline methods.
We trained models with CORAL, IRM, and Group DRO, treating each hospital as a domain.
However, they performed comparably or worse than the ERM baseline.
For the CORAL and IRM models, our grid search selected the lowest values of their penalty weights (0.1 and 1, respectively) based on OOD validation accuracy.
Figure 18:
Test (OOD) accuracy versus validation (OOD) accuracy for different random seeds on Camelyon17-wilds, using the same hyperparameters. The test accuracy is far more variable than the validation accuracy (note the differences in the axes), in part because we early stop on the highest OOD validation accuracy.
##### Discussion.
These results demonstrate a subtle failure mode when considering out-of-distribution accuracy: there are models (i.e., choices of hyperparameters and random seeds) that do well both in- and out-of-distribution, but we cannot reliably choose these models from just the training/validation set.
Due to the substantial variability in test accuracy on Camelyon17-wilds (see Figure [18](#S5.F18 "Figure 18 ‣ Additional baseline methods. ‣ E.2.2 Baseline results ‣ E.2 Camelyon17-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), we ask researchers to submit leaderboard submissions with results from 10 random seeds, instead of the 3 random seeds required for other datasets.
Many specialized methods have been developed to handle stain variation in the context of digital histopathology. These typically fall into one of two categories: data augmentation methods that perturb the colors in the training images (e.g., Liu et al. ([2017](#bib.bib244)); Bug et al. ([2017](#bib.bib65)); Tellez et al. ([2018](#bib.bib369)))
or stain normalization methods that seek to standardize colors across training images (e.g., Macenko et al. ([2009](#bib.bib253)); BenTaieb and Hamarneh ([2017](#bib.bib44))).
These methods are reasonably effective at mitigating stain variation, at least in some contexts (Tellez et al., [2019](#bib.bib370); Miller et al., [2021](#bib.bib265)), though the general problem of learning digital histopathology models that can be effectively deployed across multiple hospitals/sites is still an open challenge.
To facilitate more controlled experiments, we will have two leaderboard tracks for Camelyon17-wilds.
For the first track, which focuses on general-purpose algorithms, submissions should not use color-specific techniques (e.g., color augmentation) and should also train their models from scratch, instead of fine-tuning models that are pre-trained from ImageNet or other datasets.
For the second track, submissions can use any of those techniques, including specialized methods for dealing with stain variation.
These separate tracks will help to disentangle the contributions of more general-purpose learning algorithms and model architectures from the contributions of specialized augmentation techniques or additional training data.
####
E.2.3 Broader context
Other than stain variation, there are many other distribution shifts that might occur in histopathology applications. For example, patient demographics might differ from hospital to hospital: some hospitals might tend to see patients who are older or more sick, and patients from different backgrounds and countries vary in terms of cancer susceptibility (Henderson et al., [2012](#bib.bib171)).
Some cancer subtypes and tissues of origin are also more common than others, leading to potential subpopulation shift issues, e.g,. a rare cancer subtype in one context might be more common in another; or even if it remains rare, we would seek to leverage the greater quantity of data from other subtypes to improve model accuracy on the rare subtype (Weinstein et al., [2013](#bib.bib400)).
Beyond histopathology, variation between different hospitals and deployment sites has also been shown to degrade model accuracy in other medical applications such as diabetic retinopathy (Beede et al., [2020](#bib.bib35)) and chest radiographs (Zech et al., [2018](#bib.bib427); Phillips et al., [2020](#bib.bib294)), including recent work on COVID-19 detection (DeGrave et al., [2020](#bib.bib107)).
Even within the same hospital, process variables like which scanner/technician took the image can significantly affect models (Badgeley et al., [2019](#bib.bib24)).
In these medical applications, the gold standard is to evaluate models on an independent test set collected from a different hospital (e.g., Beck et al. ([2011](#bib.bib33)); Liu et al. ([2017](#bib.bib244)); Courtiol et al. ([2019](#bib.bib96)); McKinney et al. ([2020](#bib.bib261))) or at least with a different scanner within the same hospital (e.g., Campanella et al. ([2019](#bib.bib73))).
However, this practice has not been ubiquitous due to the difficulty of obtaining data spanning multiple hospitals (Esteva et al., [2017](#bib.bib125); Bejnordi et al., [2017](#bib.bib40); Codella et al., [2019](#bib.bib86); Veta et al., [2019](#bib.bib388)).
The baseline results reported above show that even evaluating on a single different hospital might be insufficient, as results can vary widely between different hospitals (e.g., between the validation and test OOD datasets).
We hope that the Camelyon17-wilds dataset, which has multiple hospitals in the training set and independent hospitals in the validation and test sets, will be useful for developing models that can generalize reliably to new hospitals and contexts (Chen et al., [2020](#bib.bib79)).
####
E.2.4 Additional details
##### Data processing.
The Camelyon17-wilds dataset is adapted from whole-slide images (WSIs) of breast cancer metastases in lymph nodes sections, obtained from the CAMELYON17 challenge (Bandi et al., [2018](#bib.bib28)).
Each split is balanced to have an equal number of positive and negative examples.
The varying number of patches per slide and hospital is due to this class balancing, as some slides have fewer tumor (positive) patches.
We selected the test set hospital as the one whose patches were visually most distinct; the difference in test versus OOD validation performance shows that the choice of OOD hospital can significantly affect performance.
From these WSIs, we extracted patches in a standard manner, similar to Veeling et al. ([2018](#bib.bib385)).
The WSIs were scanned at a resolution of 0.23μ𝜇\muitalic\_μm–0.25μ𝜇\muitalic\_μm in the original dataset, and each WSI contains multiple resolution levels, with approximately 10,000×\times×20,000 pixels at the highest resolution level
(Bandi et al., [2018](#bib.bib28)).
We used the third-highest resolution level, corresponding to reducing the size of each dimension by a factor of 4.
We then tiled each slide with overlapping 96×\times×96 pixel patches with a step size of 32 pixels in each direction (such that none of the central 32×\times×32 regions overlap), labeling them as the following:
* •
*Tumor* patches have at least one pixel of tumor tissue in the central 32×\times×32 region. We used the pathologist-annotated tumor annotations provided with the WSIs.
* •
*Normal* patches have no tumor and have at least 20% normal tissue in the central 32×\times×32 region. We used Otsu thresholding to distinguish normal tissue from background.
We discarded all patches that had no tumor and <20% normal tissue in the central 32×\times×32 region.
To maintain an equal class balance, we then subsampled the extracted patches in the following way.
First, for each WSI, we kept all tumor patches unless the WSI had fewer normal than tumor patches, which was the case for a single WSI; in that case, we randomly discarded tumor patches from that WSI until the numbers of tumor and normal patches were equal.
Then, we randomly selected normal patches for inclusion such that for each hospital and split, there was an equal number of tumor and normal patches.
##### Modifications to the original dataset.
The task in the original CAMELYON17 challenge (Bandi et al., [2018](#bib.bib28)) was the patient-level classification task of determining the pathologic lymph node stage of the tumor present in all slides from a patient. In contrast, our task is a lesion-level classification task. Patient-level, slide-level, and lesion-level tasks are all common in histopathology applications.
As mentioned above, the original dataset provided WSIs and tumor annotations,
but not a standardized set of patches, which we provide here.
Moreover, it did not consider distribution shifts; both of the original training and test splits contained slides from all 5 hospitals.
The Camelyon17-wilds patch-based dataset is similar to one of the datasets used in Tellez et al. ([2019](#bib.bib370)), which was also derived from the CAMELYON17 challenge; there, only one hospital is used as the training set, and the other hospitals are all part of the test set.
Camelyon17-wilds is also similar to PCam (Veeling et al., [2018](#bib.bib385)), which is a patch-based dataset based on an earlier CAMELYON16 challenge; the data there is derived from only two hospitals.
##### Additional data sources.
The full, original CAMELYON17 dataset contains 1000 WSIs from the same 5 hospitals, although only 50 of them (which we use here) have tumor annotations. The other 950 WSIs may be used as unlabeled data. Beyond the CAMELYON17 dataset, the largest source of unlabeled WSI data is the Cancer Genome Atlas (Weinstein et al., [2013](#bib.bib400)), which typically has patient-level annotations (e.g., patient demographics and clinical outcomes).
###
E.3 RxRx1-wilds
High-throughput screening techniques that can generate large amounts of data
are now common in many fields of biology,
including transcriptomics (Harrill et al., [2019](#bib.bib165)),
genomics (Echeverri and Perrimon, [2006](#bib.bib121); Zhou et al., [2014](#bib.bib434)), proteomics and
metabolomics (Taylor et al., [2021](#bib.bib368)), and drug
discovery (Broach et al., [1996](#bib.bib60); Macarron et al., [2011](#bib.bib252); Swinney and Anthony, [2011](#bib.bib361); Boutros et al., [2015](#bib.bib57)).
Such large volumes of data, however, need to be created in experimental batches, or groups of experiments executed at similar times under similar conditions.
Despite attempts to carefully control experimental variables such as
temperature, humidity, and reagent concentration, measurements from
these screens are confounded by technical artifacts that arise from differences
in the execution of each batch.
These *batch effects* make it difficult to draw conclusions from data across experimental batches (Leek et al., [2010](#bib.bib228); Parker and Leek, [2012](#bib.bib287); Soneson et al., [2014](#bib.bib349); Nygaard et al., [2016](#bib.bib278); Caicedo et al., [2017](#bib.bib70)).
We study the shift induced by batch effects on a variant of the RxRx1-wilds dataset (Taylor et al., [2019](#bib.bib367)).
As illustrated in Figure [5](#S4.F5 "Figure 5 ‣ 4.1.3 RxRx1-wilds: Genetic perturbation classification across experimental batches ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), there are significant visual
differences between experimental batches, making recognizing siRNA perturbations
in OOD experiments in the RxRx1-wilds dataset a particularly challenging task for
existing ML algorithms.
####
E.3.1 Setup
##### Problem setting.
We consider the domain generalization setting, where the domains are
experimental batches and we seek to generalize to images from unseen experimental
batches. Concretely, the input x𝑥xitalic\_x is a 3-channel image of cells obtained by
fluorescent microscopy, the label y𝑦yitalic\_y indicates which of the 1,139 genetic
treatments (including no treatment) the cells received, and the domain d𝑑ditalic\_d
specifies the experimental batch of the image.
##### Data.
RxRx1-wilds was created by Recursion (recursion.com) in its automated high-throughput
screening laboratory in Salt Lake City, Utah. It is comprised of fluorescent microscopy images of
human cells in four different cell lines: HUVEC, RPE, HepG2, and U2OS. These
were acquired via fluorescent microscopy using a 6-channel variant of the
*Cell Painting* assay (Bray et al., [2016](#bib.bib59)).
Figure [19](#S5.F19 "Figure 19 ‣ Data. ‣ E.3.1 Setup ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows an example of the cellular contents of each of
these 6 channels: nuclei, endoplasmic reticuli, actin, nucleoli and cytoplasmic
RNA, mitochondria, and Golgi.
To make the dataset smaller and more accessible, we only included the first 3 channels in RxRx1-wilds.
Figure 19: 6-channel composite image of HUVEC cells (left) and its
individual channels (rest): nuclei (blue), endoplasmic reticuli (green),
actin (red), nucleoli and cytoplasmic RNA (cyan), mitochondria (magenta),
and Golgi (yellow). The overlap in channel content is due in part to the
lack of complete spectral separation between fluorescent stains. Note that
only the first 3 channels are included in RxRx1-wilds.
The images in RxRx1-wilds are the result of executing the same experimental
design 51 different times, each in a different batch of experiments. The design
consists of four 384-well plates, where individual wells are used to isolate
populations of cells on each plate (see Figure [20](#S5.F20 "Figure 20 ‣ Data. ‣ E.3.1 Setup ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
Figure 20: Schematic of a 384-well plate demonstrating imaging sites and
6-channel images. The 4-plate experiments in RxRx1-wilds were run in the wells
of such 384-well plates. RxRx1-wilds contains two imaging sites per well.
The wells are laid out in a 16×\times×24 grid, but only the wells in the inner
14×\times×22 grid are used since the outer wells are most susceptible to
environmental factors. Of these 308 usable wells, one is left untreated to
provide a *negative control* phenotype, while the rest are treated with
small interfering ribonucleic acid, or siRNA, at a fixed concentration. Each
siRNA is designed to knockdown a single target gene via the RNA interference
pathway, reducing the expression of the gene and its associated
protein (Tuschl, [2001](#bib.bib378)). However, siRNAs are known to have significant but
consistent off-target effects via the microRNA pathway, creating partial
knockdown of many other genes as well. The overall effect of siRNA transfection
is to perturb the morphology, count, and distribution of cells, creating a
*phenotype* associated with each siRNA. The phenotype is sometimes visually
recognizable, but often the effects are subtle and hard to detect.
In each plate, 30 wells are set aside for 30 *positive control* siRNAs. Each has a different gene as its primary target, which together with the
single untreated well already mentioned, provides a set of reference phenotypes
per plate. Each of the remaining 1,108 wells of the design (277 wells ×\times× 4
plates) receives one of 1,108 *treatment* siRNA, respectively, so that
there is at most one well of each treatment siRNA in each experiment. We say
at most once because, although rare, it happens that either an siRNA is not
correctly transferred into the designated destination well, resulting in an
additional untreated well, or an operational error is detected by quality
control procedures that render the well unsuitable for inclusion in the dataset.
Each experiment was run in a single cell type, and of the 51 experiments in RxRx1-wilds, 24 are in HUVEC, 11 in RPE, 11 in HepG2, and 5 in U2OS.
Figure [21](#S5.F21 "Figure 21 ‣ Data. ‣ E.3.1 Setup ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows the phenotype of the same siRNA in each of these
four cell types.
Figure 21: Images of the same siRNA in four cell types, from left to right: HUVEC, RPE, HepG2, U2OS.
We split the dataset by experimental batches, with the training and test splits having roughly the same composition of cell types:
1. 1.
Training: 33 experiments (16 HUVEC, 7 RPE, 7 HepG2, 3 U2OS),
site 1 only = 40,612 images.
2. 2.
Validation (OOD): 4 experiments (1 HUVEC, 1 RPE, 1 HepG2, 3
U2OS), sites 1 and 2 = 9,854 images.
3. 3.
Test (OOD): 14 experiments (7 HUVEC, 3 RPE, 3 HepG2, 1
U2OS), sites 1 and 2 = 34,432 images.
4. 4.
Test (ID): same 33 experiments as in the training set, site 2
only = 40,612 images.
In addition to the class (siRNA), each image is associated with the following
metadata: cell type, experiment, plate, well, and site.
We emphasize that all the images of an experiment are found in exactly one of
the training, validation (OOD) or test (OOD) splits. See
Appendix [E.3.4](#S5.SS3.SSS4 "E.3.4 Additional details ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more data processing details.
##### Evaluation.
We evaluate models by their average accuracy across test images. Note that there
are two images per well in the test set, which we evaluate independently.
The cell types are not balanced in the training and test sets.
Correspondingly, we observed higher performance on the HUVEC cell type, which is over-represented, and lower performance on the U2OS cell type, which is under-represented.
While maintaining high performance on minority (or even unseen) cell types is an important problem, for RxRx1-wilds, we opt to measure the average accuracy across all experiments instead of, for example, the worst accuracy across cell types.
This is because the relatively small amount of training data available from the minority cell type (U2OS) makes it challenging to cast RxRx1-wilds as a tractable subpopulation shift problem.
We also note that the difference in performance across cell types leads to the validation performance being significantly lower than the test performance, as there is a comparatively smaller fraction of HUVEC and a comparatively higher fraction of U2OS.
##### Potential leverage.
By design, there is usually one sample per class per experiment in the training
set, with the following exceptions: 1) there are usually four samples per
positive control, though 2) samples may be missing, as described above.
Moreover, while batch effects can manifest themselves in many complicated ways,
it is the case that the training set consists of a large number of experiments
selected randomly amongst all experiments in the dataset, hence we
expect models to be able to learn what is common amongst all such samples per
cell type, and for that ability to generalize to to test batches. We emphasize
that, whether in the training or test sets, the same cell types are perturbed
with the same siRNA, and thus the phenotypic distributions for each batch share
much of the same generative process.
We also note that, while not exploited here, there is quite a bit of structure
in the RxRx1-wilds dataset. For example, except in the case of errors, all treatment
siRNA appear once in each experiment, and all control conditions appear once per
plate, so four times per experiment. Also, due to the operational efficiencies
gained, the 1,108 treatment siRNAs always appear in the same four groups of 277
per experiment. So while the particular well an siRNA appears in is randomized,
it will always appear with the same group of 276 other siRNAs. This structure
can be exploited for improving predictive accuracy via post-prediction methods
such as linear sum assignment. However, such methods do not represent improved
generalization to OOD samples, and should be avoided.
####
E.3.2 Baseline results
##### Model.
For all experiments, we train the standard ResNet-50 model
(He et al., [2016](#bib.bib167)) pretrained on ImageNet, using a learning rate of 1e−41𝑒41e-41 italic\_e - 4 and
L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strength of 1e−51𝑒51e-51 italic\_e - 5. We trained these models with the Adam
optimizer, using default parameter values β1=0.9subscript𝛽10.9\beta\_{1}=0.9italic\_β start\_POSTSUBSCRIPT 1 end\_POSTSUBSCRIPT = 0.9 and β2=0.999subscript𝛽20.999\beta\_{2}=0.999italic\_β start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT = 0.999, with a batch size of 75 for 90 epochs, linearly increasing the learning
rate for 10 epochs, then decreasing it following a cosine learning rate schedule.
We selected hyperparameters by a grid search over learning rates {10−5\{10^{-5}{ 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT, 10−4superscript10410^{-4}10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT, 10−3}10^{-3}\}10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT }, L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strengths {10−5,10−3}superscript105superscript103\{10^{-5},10^{-3}\}{ 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT },
and numbers of warmup epochs {5,10}510\{5,10\}{ 5 , 10 }.
We report results aggregated over 3 random seeds.
##### ERM results and performance drops.
Model performance dropped significantly going from the train-to-train in-distribution (ID) setting to
the official out-of-distribution (OOD) setting (Table [7](#S5.T7 "Table 7 ‣ ERM results and performance drops. ‣ E.3.2 Baseline results ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")),
with an average accuracy of 35.9% on the ID test set but only 29.9% on the OOD test set for ERM.
Table 7: Baseline results on RxRx1-wilds. In-distribution (ID) results correspond to the train-to-train setting. Parentheses show standard deviation across
3 replicates.
| | | | |
| --- | --- | --- | --- |
| Algorithm | Validation (OOD) accuracy | Test (ID) accuracy | Test (OOD) accuracy |
| ERM | 19.4 (0.2) | 35.9 (0.4) | 29.9 (0.4) |
| CORAL | 18.5 (0.4) | 34.0 (0.3) | 28.4 (0.3) |
| IRM | 5.6 (0.4) | 9.9 (1.4) | 8.2 (1.1) |
| Group DRO | 15.2 (0.1) | 28.1 (0.3) | 23.0 (0.3) |
Table 8: Mixed-to-test comparison for ERM models on RxRx1-wilds.
In the official OOD setting, we train on data from 33 experiments (1 site per experiment) and test on 14 different experiments (2 sites per experiment).
In the mixed-to-test setting, we replace 14 of the training experiments with 1 site from each of the test experiments, which keeps the training set size the same, but halves the test set size.
Parentheses show standard deviation across 3 replicates.
| | | |
| --- | --- | --- |
| Setting | Algorithm | Test (OOD) accuracy |
| Official (train on ID examples) | ERM | 29.9 (0.4) |
| Mixed-to-test (train on ID + OOD examples) | ERM | 39.8 (0.2) |
We ran an additional mixed-to-test comparison, where we moved half of the OOD test set into the training set, while keeping the overall amount of training data the same.
Specifically, we moved one site per experiment from the OOD test set into the training set, and discarded an equivalent number of training sites, while leaving the validation set unchanged.
While the test set in the mixed-to-test setting is effectively half as large as in the standard split, we expect it to be distributed similarly, since the two test set versions comprise the same 14 experiments.
Table [8](#S5.T8 "Table 8 ‣ ERM results and performance drops. ‣ E.3.2 Baseline results ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that there is a large gap between the OOD test accuracies in the official setting (29.9%) and the test accuracies in the mixed-to-test setting (39.8%).
We note that the latter is higher than the train-to-train ID test accuracy of 35.9% reported in Table [7](#S5.T7 "Table 7 ‣ ERM results and performance drops. ‣ E.3.2 Baseline results ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
This difference mainly stems from the slight difference in cell type composition between the test sets in the train-to-train and mixed-to-test settings; in particular, the train-to-train test set has a slightly higher proportion of the minority cell type (U2OS), on which performance is worse, and a slightly lower proportion of the majority cell type (HUVEC), on which performance is better.
In this sense, the mixed-to-test result of 39.8% is a more accurate reflection of in-distribution performance on this dataset, and the results in Table [7](#S5.T7 "Table 7 ‣ ERM results and performance drops. ‣ E.3.2 Baseline results ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") therefore understate the magnitude of the distribution shift.
##### Additional baseline methods.
We also trained models with CORAL, IRM, and group DRO, treating each experiment
as a domain, and using the same model hyperparameters as ERM.
However, the models trained using these methods all performed poorly compared to the ERM model (Table [7](#S5.T7 "Table 7 ‣ ERM results and performance drops. ‣ E.3.2 Baseline results ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
One complication with these methods is that the experiments in the training set comprise different cell types, as mentioned above; this heterogeneity can pose a challenge to methods that treat each domain equivalently.
##### Discussion.
An important observation about batch effects in biological experiments: it is
often the case that batch effects are mediated via biological mechanisms. For
example, an increase in cellular media concentration may lead to cell growth and
proliferation, while the upregulation of proliferation genes will do the same.
Thus the “nuisance” factors associated with batch effects are often correlated
with the biological signal we are attempting to observe, and cannot be
disentangled from the biological factors that explain the data. Correction algorithms
should take account of such trade-offs and attempt to optimize for both
correction and signal preservation.
####
E.3.3 Broader context
As previously mentioned, high-throughput screening techniques are used broadly
across many areas of biology, and therefore batch effects are a common problem
in fields such as genomics, transcriptomics, proteomics, metabolomics, etc., so
a particular solution in one such area may prove to be applicable in many areas
of biology (Goh et al., [2017](#bib.bib152)).
There are other datasets that are used in studying batch effects. The one most
comparable to RxRx1-wilds is the BBBC021 dataset (Ljosa et al., [2012](#bib.bib245)), which
contains 13,200 3-channel fluorescent microscopy images of MCF7 cells acquired
across 10 experimental batches. A subset of 103 treatments from 38 drug
compounds belonging to 12 known mechanism of action (MoA) groups was first
studied in Ando et al. ([2017](#bib.bib14)), and has been the subject of subsequent
studies (Caicedo et al., [2018](#bib.bib71); Godinez et al., [2018](#bib.bib148); Tabak et al., [2020](#bib.bib362)).
Note that this dataset differs dramatically from RxRx1, in that there are fewer
images, treatments, batches, and cell types, and each batch contains only a
small subset of the total treatments.
####
E.3.4 Additional details
##### Data processing.
RxRx1-wilds contains two non-overlapping 256×\times×256 fields of view per well.
Therefore, there could be as many as 125,664 images in the dataset (= 51 experiments ×\times× 4 plates/experiment ×\times× 308 wells/plate ×\times× 2 images/well).
154 images were removed based on data quality, leaving a total dataset of 125,510 images.
##### Modifications to the original dataset.
The underlying raw dataset
consists of 2048 ×\times× 2048 pixel, 6 channel, 16bpp images. To fit within the
constraints of the Wilds benchmark, images for RxRx1-wilds were first downsampled to
1024 ×\times× 1024 and 8bpp, cropped to the center 256 ×\times× 256 pixels, and only the
first three channels (nuclei, endoplasmic reticuli, actin) were retained. The
original RxRx1 dataset, available at rxrx.ai and described in Taylor et al. ([2019](#bib.bib367)), provides 512 ×\times× 512 center
crops of the downsampled images with all 6 channels retained.
The original RxRx1 dataset was also used in a NeurIPS 2019 competition hosted on Kaggle. The validation (OOD) and test (OOD) splits in RxRx1-wilds correspond to the public and private test sets from the Kaggle competition. The original RxRx1 dataset did not have an additional test (ID) split, and thus the original training split had both sites 1 and 2, for a total of 81,442 images.
The Kaggle competition also aggregated predictions from both sites to form a single prediction per well, whereas in RxRx1-wilds, we treat each site separately.
As described in Section [E.3.1](#S5.SS3.SSS1 "E.3.1 Setup ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), each plate in both the training and test sets contains the
same 31 control conditions (one untreated well, and 30 positive control siRNAs).
The Kaggle competition provided the labels for these control conditions in the test set, expecting that competitors would use them for various domain alignment techniques such as CORAL. However, these labels were instead used by the top competitors to bootstrap pseudo-labeling techniques.
For RxRx1-wilds, for consistency with the other datasets and the typical domain generalization setting, we have opted not to release these control test labels for training.
The poor performance reported here on RxRx1-wilds may seem
surprising in light of the fact that the top finishers of the Kaggle
competition achieved near perfect accuracy on the test (OOD) set. This difference is due to a number of factors, including:
1. 1.
Adjustments made to the original RxRx1 dataset for RxRx1-wilds, as detailed in this subsection.
2. 2.
Differences in the network architectures used. To make training on RxRx1-wilds more accessible, we used a less compute-intensive architecture than typical in the competition.
3. 3.
Differences in training techniques used like pseudo-labeling (using the test control labels, as described above) and batch-level dataset augmentations or ensembling.
4. 4.
Differences in the way accuracy is measured. In the Kaggle competition, accuracy was measured for each well, meaning site-level predictions were aggregated to well-level predictions, and only for treatment classes, whereas in RxRx1-wilds, for convenience, accuracy is measured at each site and for both treatment and control classes.
5. 5.
The use of post-prediction methods like linear sum assignment that exploited the particular structure of the experiments in the RxRx1 dataset, as described under Potential Leverage in Section [E.3.1](#S5.SS3.SSS1 "E.3.1 Setup ‣ E.3 RxRx1-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
###
E.4 OGB-MolPCBA
Accurate prediction of the biochemical properties of small molecules can significantly accelerate drug discovery by reducing the need for expensive lab experiments (Shoichet, [2004](#bib.bib346); Hughes et al., [2011](#bib.bib184)).
However, the experimental data available for training such models is limited compared to the extremely diverse and combinatorially large universe of candidate molecules that we would want to make predictions on (Bohacek et al., [1996](#bib.bib52); Sterling and Irwin, [2015](#bib.bib352); Lyu et al., [2019](#bib.bib251); McCloskey et al., [2020](#bib.bib258)).
This means that models need to generalize to out-of-distribution molecules that are structurally different from those seen in the training set.
We study this issue through the OGB-MolPCBA dataset, which is directly adopted from the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)) and originally curated by MoleculeNet (Wu et al., [2018](#bib.bib412)).
####
E.4.1 Setup
##### Problem setting.
We consider the domain generalization setting, where the domains are molecular scaffolds, and our goal is to learn models that generalize to structurally distinct molecules with scaffolds that are not in the training set (Figure [6](#S4.F6 "Figure 6 ‣ 4.1.4 OGB-MolPCBA: Molecular property prediction across different scaffolds ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
This is a multi-task classification problem: for each molecule, we predict the presence or absence of 128 kinds of biological activities, such as binding to a particular enzyme.
In addition, we cluster the molecules into different scaffold groups according to their two-dimensional structure, and annotate each molecule with the scaffold group that it belongs to.
Concretely, the input x𝑥xitalic\_x is a molecular graph, the label y𝑦yitalic\_y is a 128-dimensional binary vector where each component corresponds to a biochemical assay result, and the domain d𝑑ditalic\_d specifies the scaffold. Not all biological activities are measured for each molecule, so y𝑦yitalic\_y can have missing values.
##### Data.
OGB-MolPCBA contains more than 400K small molecules with 128 kinds of prediction labels.
Each small molecule is represented as a graph, where the nodes are atoms and the edges are chemical bonds.
The molecules are pre-processed using RDKit (Landrum et al., [2006](#bib.bib220)).
Input node features are 9-dimensional, including atomic number, chirality, whether the atom is in the ring. Input edge features are 3-dimensional, including bond type and bond stereochemistry.
We split the dataset by scaffold structure. This *scaffold split* (Wu et al., [2018](#bib.bib412)) is also used in the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)).
By attempting to separate structurally different molecules into different subsets, it provides a realistic estimate of model performance in prospective experimental settings.
We assign the largest scaffolds to the training set to make it easier for algorithms to leverage scaffold information, and the smallest scaffolds to the test set to ensure that it is maximally diverse in scaffold structure:
1. 1.
Training: The largest 44,930 scaffolds, with an average of 7.8 molecules per scaffold.
2. 2.
Validation (OOD): The next largest 31,361 scaffolds, with an average of 1.4 molecules per scaffold.
3. 3.
Test (OOD): The smallest 43,793 scaffolds, which are all singletons.
In Figure [22](#S5.F22 "Figure 22 ‣ Data. ‣ E.4.1 Setup ‣ E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") (A), we plot the statistics of the scaffolds in terms of the number of molecules belonging to each scaffold. We see that the scaffold sizes are highly skewed, with the test set containing (by design) the scaffolds with the least molecules.
However, the differences in scaffold sizes do not significantly change the statistics of the molecules in each split.
In Figures [22](#S5.F22 "Figure 22 ‣ Data. ‣ E.4.1 Setup ‣ E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") (B) and (C), we see that the label statistics remain very similar across train/validation/test splits, suggesting that the main distribution shift comes from the difference in the input molecular graph structure.
Figure 22: Analyses of scaffold groups in the OGB-MolPCBA dataset. (A) shows the distribution of the scaffold sizes, (B) and (C) show how the ratios of positive molecules and labeled molecules for the 128 tasks vary across the train/validation /test splits.
##### Evaluation.
We evaluate models by their average Average Precision (AP) across tasks (i.e., we compute the average precision for each task separately, and then average those scores), following Hu et al. ([2020b](#bib.bib182)). This accounts for the extremely skewed class balance in OGB-MolPCBA (only 1.4% of data is positive). Not all labels are available for each molecule; when calculating the AP for each task, we only consider the labeled molecules for the task.
##### Potential leverage.
We provide the scaffold grouping of molecules for training algorithms to leverage. Finding generalizable representations of molecules across different scaffold groups is useful for models to make accurate extrapolation on unseen scaffold groups. In fact, very recent work (Jin et al., [2020](#bib.bib189)) has leveraged scaffold information of molecules to improve the extrapolation performance of molecular property predictors.
One notable characteristic of the scaffold group is that the size of each group is rather small; on the training split, each scaffold contains only 7.8 molecules on average. This also results in many scaffold groups: 44,930 groups in the training split. In Figure [22](#S5.F22 "Figure 22 ‣ Data. ‣ E.4.1 Setup ‣ E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we show that these scaffold groups are well-behaved in the sense that the train/validation/test splits contain contain similar ratios of positive labels as well as missing labels.
Table 9: Baseline results on OGB-MolPCBA. Parentheses show standard deviation across 3 replicates.
| | | |
| --- | --- | --- |
| Algorithm | Validation AP (%) | Test AP (%) |
| ERM | 27.8 (0.1) | 27.2 (0.3) |
| CORAL | 18.4 (0.2) | 17.9 (0.5) |
| IRM | 15.8 (0.2) | 15.6 (0.3) |
| Group DRO | 23.1 (0.6) | 22.4 (0.6) |
Table 10:
Random split comparison for ERM models on OGB-MolPCBA.
In the official OOD setting, we train on molecules from some scaffolds and evaluate on molecules from different scaffolds, whereas in the random split setting, we randomly divide molecules into training and test sets without using scaffold information.
Parentheses show standard deviation across 3 replicates.
| | | |
| --- | --- | --- |
| Setting | Algorithm | Test AP (%) |
| Official (split by scaffolds) | ERM | 27.2 (0.3) |
| Random split (split i.i.d.) | ERM | 34.4 (0.9) |
####
E.4.2 Baseline results
##### Model.
For all experiments, we use Graph Isomorphism Networks (GIN) (Xu et al., [2018](#bib.bib418)) combined with virtual nodes (Gilmer et al., [2017](#bib.bib147)), as this is currently the model with the highest performance in the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)).
We follow the same hyperparameters as in the Open Graph Benchmark: 5 GNN layers with a dimensionality of 300;
the Adam optimizer (Kingma and Ba, [2015](#bib.bib207)) with a learning rate of 0.001;
and training for 100 epochs with early stopping.
For each of the baseline algorithms (ERM, CORAL, IRM, and Group DRO),
we separately tune the dropout rate from {0,0.5}00.5\{0,0.5\}{ 0 , 0.5 };
in addition, for CORAL and IRM, we tune the penalty weight as in Appendix [D](#S4a "D Additional experimental details ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
##### ERM results and performance drops.
We first compare the generalization performance of ERM on the official scaffold split against the conventional random split, in which the entire molecules are randomly split into train/validation/test sets with the same split ratio as the scaffold split (i.e., 80/10/10).
Results are in Table [10](#S5.T10 "Table 10 ‣ Potential leverage. ‣ E.4.1 Setup ‣ E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"). The test performance of ERM drops by 7.2 points AP when the scaffold split is used, suggesting that the scaffold split is indeed harder than the random split.
To maintain consistency with the Open Graph Benchmark, and because the number of examples (molecules) per domain (scaffold) is relatively small compared to other datasets, we opted not to split off a portion of the training set into Validation (ID) and Test (ID) sets.
We therefore do not run a train-to-train comparison for OGB-MolPCBA.
Moreover, as the official scaffold split assigns the largest scaffolds to the training set and the smallest scaffolds to the test set, the test scaffolds all only have one molecule per scaffold, which precludes running test-to-test and mixed-to-test comparisons.
A potential issue with the random split ID comparison is that it does not measure performance on the same test distribution as the official split, and therefore might be confounded by differences in intrinsic difficulty. However, we believe that the random split setting provides a reasonable measure of ID performance for OGB-MolPCBA, as Figure [22](#S5.F22 "Figure 22 ‣ Data. ‣ E.4.1 Setup ‣ E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that the distribution of scaffolds assigned to the training versus test sets are similar. As the random split contains many singleton scaffolds in its test set that do not have corresponding molecules in the training set, we believe that it is likely to be an underestimate of the ID-OOD gap in OGB-MolPCBA.
##### Additional baseline methods.
Table [9](#S5.T9 "Table 9 ‣ Potential leverage. ‣ E.4.1 Setup ‣ E.4 OGB-MolPCBA ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") also shows that ERM performs better than CORAL, IRM, and Group DRO, all of which use scaffolds as the domains. For CORAL and IRM, we find that smaller penalties give better generalization performance, as larger penalty terms make the training insufficient.
We use the 0.10.10.10.1 penalty for CORAL and λ=1𝜆1\lambda=1italic\_λ = 1 for IRM.
The primary issue with these existing methods is that they make the model significantly underfit the training data even when dropout is turned off.
For instance, the training AP of CORAL and IRM is 20.0% and 15.9%, respectively, which are both lower than the 36.1% that ERM obtains even with 0.5 dropout.
Also, these methods are primarily designed for the case when each group contains a decent number of examples, which is not the case for the OGB-MolPCBA dataset.
####
E.4.3 Broader context
Because of the very nature of discovering *new* molecules, out-of-distribution prediction is prevalent in nearly all applications of machine learning to chemistry domains. Beyond drug discovery, a variety of tasks and their associated datasets have been proposed for molecules of different sizes.
For small organic molecules, the scaffold split has been widely adopted to stress-test models’ capability for out-of-distribution generalization. While OGB-MolPCBA primarily focuses on predicting biophysical activity (e.g., protein binding), other datasets in MoleculeNet (Wu et al., [2018](#bib.bib412)) include prediction of quantum mechanical properties (e.g., HOMO/LUMO), physical chemistry properties (e.g., water solubility), and physiological properties (e.g., toxicity prediction (Attene-Ramos et al., [2013](#bib.bib18))).
Besides small molecules, it is also of interest to apply machine learning over larger molecules such as catalysts and proteins.
In the domain of catalysis, using machine learning to approximate expensive quantum chemistry simulation has gotten attention. The OC20 dataset has been recently introduced, containing 200+ million samples from quantum chemistry simulations relevant to the discovery of new catalysts for renewable energy storage and other energy applications (Becke, [2014](#bib.bib34); Chanussot et al., [2020](#bib.bib77); Zitnick et al., [2020](#bib.bib435)). The OC20 dataset explicitly provides test sets with qualitatively different materials.
In the domain of proteins, the recent trend is to use machine learning to predict 3D structure of proteins given their amino acid sequence information. This is known as the protein folding problem, and has sometimes been referred to as the Holy Grail of structural biology (Dill and MacCallum, [2012](#bib.bib111)).
CASP is a bi-annual competition to benchmark the progress of protein folding (Moult et al., [1995](#bib.bib269)), and it evaluates predictions made on proteins whose 3D structures are identified very recently, presenting a natural temporal distribution shift.
Recently, the AlphaFold2 deep learning model obtained breakthrough performance on the CASP challenge (Jumper et al., [2020](#bib.bib193)), demonstrating exciting avenues of machine learning for structural biology.
####
E.4.4 Additional details
Data processing.
The OGB-MolPCBA dataset contains 437,929 molecules annotated with 128 kinds of labels, each representing a bioassay curated in the PubChem database (Kim et al., [2016b](#bib.bib206)). More details are provided in the MoleculeNet (Wu et al., [2018](#bib.bib412)) and the Open Graph Benchmark (Hu et al., [2020b](#bib.bib182)), from which the dataset is adopted.
###
E.5 GlobalWheat-wilds
Models for automated, high-throughput plant phenotyping—measuring the physical characteristics of plants and crops, such as wheat head density and counts—are important tools for crop breeding (Thorp et al., [2018](#bib.bib372); Reynolds et al., [2020](#bib.bib313)) and agricultural field management (Shi et al., [2016](#bib.bib342)).
These models are typically trained on data collected in a limited number of regions, even for crops grown worldwide such as wheat (Madec et al., [2019](#bib.bib254); Xiong et al., [2019](#bib.bib417); Ubbens et al., [2020](#bib.bib381); Ayalew et al., [2020](#bib.bib22)).
However, there can be substantial variation between regions, due to differences in crop varieties, growing conditions, and data collection protocols.
Prior work on wheat head detection has shown that this variation can significantly degrade model performance on regions unseen during training (David et al., [2020](#bib.bib104)).
We study this shift in an expanded version of the Global Wheat Head Dataset (David et al., [2020](#bib.bib104), [2021](#bib.bib105)), a large set of wheat images collected from 12 countries around the world.
####
E.5.1 Setup
##### Problem setting.
We consider the domain generalization setting, where the goal is to learn models that generalize to images taken from new countries and acquisition sessions (Figure [7](#S4.F7 "Figure 7 ‣ 4.1.5 GlobalWheat-wilds: Wheat head detection across regions of the world ‣ 4.1 Domain generalization datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The task is wheat head detection, which is a single-class object detection task.
Concretely, the input x𝑥xitalic\_x is an overhead outdoor image of wheat plants, and the label y𝑦yitalic\_y is a set of bounding box coordinates that enclose the wheat heads (the spike at the top of the wheat plant containing grain), excluding the hair-like awns that may extend from the head.
The domain d𝑑ditalic\_d specifies an *acquisition session*, which corresponds to a specific location, time, and sensor for which a set of images were collected.
Our goal is to generalize to new acquisition sessions that are unseen during training.
In particular, the dataset split captures a shift in location, with training and test sets comprising images from disjoint countries as discussed below.
##### Data.
The dataset comprises 6,515 images containing 275,187 wheat heads.
These images were collected over 47 acquisition sessions in 16 research institutes across 12 countries. We describe the metadata and statistics of each acquisition session in Table [11](#S5.T11 "Table 11 ‣ Data. ‣ E.5.1 Setup ‣ E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Many factors contribute to the variation in wheat appearance across acquisition sessions.
In particular, across locations, there is substantial variation due to differences in wheat genotypes, growing conditions (e.g., planting density), illumination protocols, and sensors.
We study the effect of this location shift by splitting the dataset by country
and assigning acquisition sessions from disjoint continents to the training and test splits:
1. 1.
Training: Images from 18 acquisition sessions in Europe (France ×\times×13, Norway ×\times×2, Switzerland, United Kingdom, Belgium), containing 131,864 wheat heads across 2,943 images.
2. 2.
Validation (OOD):
Images from 7 acquisition sessions in Asia (Japan ×\times× 4, China ×\times× 3) and 1 acquisition session in Africa (Sudan), containing 44,873 wheat heads across 1,424 images.
3. 3.
Test (OOD): Images from 11 acquisition sessions in Australia and 10 acquisition sessions in North America (USA ×\times× 6, Mexico ×\times× 3, Canada), containing 66,905 wheat heads across 1,434 images.
4. 4.
Validation (ID): Images from the same 18 training acquisition sessions in Europe, containing 15,733 wheat heads across 357 images.
5. 5.
Test (ID): Images from the same 18 training acquisition sessions in Europe, containing 16,093 wheat heads across 357 images.
Table 11:
Acquisition sessions in GlobalWheat-wilds. Growth stages are abbreviated as F: Filling, R: Ripening, PF: Post-flowering. Locations are abbreviated as VLB: Villiers le Bâcle, VSC: Villers-Saint-Christophe. UTokyo\_1 and UTokyo\_2 are from the same location with different cart sensors and UTokyo\_3 consists of images from a variety of farms in Hokkaido between 2016 and 2019.
The # images and # heads in the “Train” domains include the images and heads used in the Val (ID) and Test (ID) splits, which are taken from the same set of training domains. The “Val” and “Test” domains refer to the Val (OOD) and Test (OOD) splits, respectively.
| | | | | | | | | | |
| --- | --- | --- | --- | --- | --- | --- | --- | --- | --- |
| Split | Name | Owner | Country | Site | Date | Sensor | Stage | # Images | # Heads |
| Training | Ethz\_1 | ETHZ | Switzerland | Eschikon | 06/06/2018 | Spidercam | F | 747 | 49603 |
| Training | Rres\_1 | Rothamsted | UK | Rothamsted | 13/07/2015 | Gantry | F-R | 432 | 19210 |
| Training | ULiège\_1 | Uliège | Belgium | Gembloux | 28/07/2020 | Cart | R | 30 | 1847 |
| Training | NMBU\_1 | NMBU | Norway | NMBU | 24/07/2020 | Cart | F | 82 | 7345 |
| Training | NMBU\_2 | NMBU | Norway | NMBU | 07/08/2020 | Cart | R | 98 | 5211 |
| Training | Arvalis\_1 | Arvalis | France | Gréoux | 02/06/2018 | Handheld | PF | 66 | 2935 |
| Training | Arvalis\_2 | Arvalis | France | Gréoux | 16/06/2018 | Handheld | F | 401 | 21003 |
| Training | Arvalis\_3 | Arvalis | France | Gréoux | 07/2018 | Handheld | F-R | 588 | 21893 |
| Training | Arvalis\_4 | Arvalis | France | Gréoux | 27/05/2019 | Handheld | F | 204 | 4270 |
| Training | Arvalis\_5 | Arvalis | France | VLB\* | 06/06/2019 | Handheld | F | 448 | 8180 |
| Training | Arvalis\_6 | Arvalis | France | VSC\* | 26/06/2019 | Handheld | F-R | 160 | 8698 |
| Training | Arvalis\_7 | Arvalis | France | VLB\* | 06/2019 | Handheld | F-R | 24 | 1247 |
| Training | Arvalis\_8 | Arvalis | France | VLB\* | 06/2019 | Handheld | F-R | 20 | 1062 |
| Training | Arvalis\_9 | Arvalis | France | VLB\* | 06/2020 | Handheld | R | 32 | 1894 |
| Training | Arvalis\_10 | Arvalis | France | Mons | 10/06/2020 | Handheld | F | 60 | 1563 |
| Training | Arvalis\_11 | Arvalis | France | VLB\* | 18/06/2020 | Handheld | F | 60 | 2818 |
| Training | Arvalis\_12 | Arvalis | France | Gréoux | 15/06/2020 | Handheld | F | 29 | 1277 |
| Training | Inrae\_1 | INRAe | France | Toulouse | 28/05/2019 | Handheld | F-R | 176 | 3634 |
| Val | Utokyo\_1 | UTokyo | Japan | NARO-Tsukuba | 22/05/2018 | Cart | R | 538 | 14185 |
| Val | Utokyo\_2 | UTokyo | Japan | NARO-Tsukuba | 22/05/2018 | Cart | R | 456 | 13010 |
| Val | Utokyo\_3 | UTokyo | Japan | NARO-Hokkaido | 2016-19 | Handheld | multiple | 120 | 3085 |
| Val | Ukyoto\_1 | UKyoto | Japan | Kyoto | 30/04/2020 | Handheld | PF | 60 | 2670 |
| Val | NAU\_1 | NAU | China | Baima | n/a | Handheld | PF | 20 | 1240 |
| Val | NAU\_2 | NAU | China | Baima | 02/05/2020 | Cart | PF | 100 | 4918 |
| Val | NAU\_3 | NAU | China | Baima | 09/05/2020 | Cart | F | 100 | 4596 |
| Val | ARC\_1 | ARC | Sudan | Wad Medani | 03/2021 | Handheld | F | 30 | 1169 |
| Test | Usask\_1 | USaskatchewan | Canada | Saskatoon | 06/06/2018 | Tractor | F-R | 200 | 5985 |
| Test | KSU\_1 | KansasStateU | US | Manhattan, KS | 19/05/2016 | Tractor | PF | 100 | 6435 |
| Test | KSU\_2 | KansasStateU | US | Manhattan, KS | 12/05/2017 | Tractor | PF | 100 | 5302 |
| Test | KSU\_3 | KansasStateU | US | Manhattan, KS | 25/05/2017 | Tractor | F | 95 | 5217 |
| Test | KSU\_4 | KansasStateU | US | Manhattan, KS | 25/05/2017 | Tractor | R | 60 | 3285 |
| Test | Terraref\_1 | TERRA-REF | US | Maricopa | 02/04/2020 | Gantry | R | 144 | 3360 |
| Test | Terraref\_2 | TERRA-REF | US | Maricopa | 20/03/2020 | Gantry | F | 106 | 1274 |
| Test | CIMMYT\_1 | CIMMYT | Mexico | Ciudad Obregon | 24/03/2020 | Cart | PF | 69 | 2843 |
| Test | CIMMYT\_2 | CIMMYT | Mexico | Ciudad Obregon | 19/03/2020 | Cart | PF | 77 | 2771 |
| Test | CIMMYT\_3 | CIMMYT | Mexico | Ciudad Obregon | 23/03/2020 | Cart | PF | 60 | 1561 |
| Test | UQ\_1 | UQueensland | Australia | Gatton | 12/08/2015 | Tractor | PF | 22 | 640 |
| Test | UQ\_2 | UQueensland | Australia | Gatton | 08/09/2015 | Tractor | PF | 16 | 39 |
| Test | UQ\_3 | UQueensland | Australia | Gatton | 15/09/2015 | Tractor | F | 14 | 297 |
| Test | UQ\_4 | UQueensland | Australia | Gatton | 01/10/2015 | Tractor | F | 30 | 1039 |
| Test | UQ\_5 | UQueensland | Australia | Gatton | 09/10/2015 | Tractor | F-R | 30 | 3680 |
| Test | UQ\_6 | UQueensland | Australia | Gatton | 14/10/2015 | Tractor | F-R | 30 | 1147 |
| Test | UQ\_7 | UQueensland | Australia | Gatton | 06/10/2020 | Handheld | R | 17 | 1335 |
| Test | UQ\_8 | UQueensland | Australia | McAllister | 09/10/2020 | Handheld | R | 41 | 4835 |
| Test | UQ\_9 | UQueensland | Australia | Brookstead | 16/10/2020 | Handheld | F-R | 33 | 2886 |
| Test | UQ\_10 | UQueensland | Australia | Gatton | 22/09/2020 | Handheld | F-R | 106 | 8629 |
| Test | UQ\_11 | UQueensland | Australia | Gatton | 31/08/2020 | Handheld | PF | 84 | 4345 |
##### Evaluation.
We evaluate models by first computing the average accuracy of bounding box detection within each image;
then computing the average accuracy for each acquisition session by averaging its per-image accuracies;
and finally averaging the accuracies of each acquisition session.
The accuracy of a bounding box detection is measured at a fixed Intersection over Union (IoU) threshold of 0.5.
The accuracy of an image is computed as TPTP+FN+FP𝑇𝑃𝑇𝑃𝐹𝑁𝐹𝑃\frac{TP}{TP+FN+FP}divide start\_ARG italic\_T italic\_P end\_ARG start\_ARG italic\_T italic\_P + italic\_F italic\_N + italic\_F italic\_P end\_ARG, where
TP𝑇𝑃TPitalic\_T italic\_P is the number of true positives, which are ground-truth bounding boxes that can be matched with some predicted bounding box at IoU above the threshold;
FN𝐹𝑁FNitalic\_F italic\_N is the number of false negatives, which are ground-truth bounding boxes that cannot be matched as above; and
FP𝐹𝑃FPitalic\_F italic\_P is the number of false positives, which are predicted bounding boxes that cannot be matched with any ground-truth bounding box.
We use accuracy rather than average precision, which is a common metric for object detection, because it was used in previous Global Wheat Challenges with the dataset (David et al., [2020](#bib.bib104), [2021](#bib.bib105)). We use a permissive IoU threshold of 0.5 because there is some uncertainty regarding the precise outline of wheat head instances due to the stem and awns extending from the head.
We measure the average accuracy across acquisition sessions because the number of images varies significantly across acquisition sessions, from 17 to 200 images in the test set, and we use average accuracy instead of worst-case accuracy because the wheat images are more difficult for some acquisition sessions.
##### Potential leverage.
The appearance of wheat heads in the images taken from different acquisition sessions can vary significantly, due to differences in the sensors used; illumination conditions, due to differences in illumination protocols, or the time of day and time of year that the images were taken; wheat genotypes; growth stages; growing conditions; and planting strategies.
For example, different locations might feature a mix of different varieties of wheat (with different genotypes) with different appearances. Likewise, wheat planting strategies and growing conditions vary between regions and can contribute to differences between sessions, e.g., higher planting density may result in more closely packed plants and more occlusion between wheat head instances.
To provide leverage for models to learn to generalize across these conditions, we include images from 5 countries and 18 acquisition sessions in the training set.
These training sessions cover all growth stages and include significant variation among all of the other factors.
While the test domains include unseen conditions (e.g., sensors and genotypes not seen in the training set), our hope is that the variation in the training set will be sufficient to learn models that are robust to changes in these conditions.
####
E.5.2 Baseline results
##### Model.
For all experiments, we use the Faster-RCNN detection model (Ren et al., [2015](#bib.bib312)), which has been successfully applied to the wheat head localization problem (Madec et al., [2019](#bib.bib254); David et al., [2020](#bib.bib104)).
To train, we fine-tune a model pre-trained with ImageNet, using a batch size of 4, a learning rate of 10−5superscript10510^{-5}10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT, and weight decay of 10−3superscript10310^{-3}10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT for 10 epochs with early stopping.
The hyperparameters were chosen from a grid search over learning rates {10−6,10−5,10−4}superscript106superscript105superscript104\{10^{-6},10^{-5},10^{-4}\}{ 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT } and weight decays {0,10−4,10−3}0superscript104superscript103\{0,10^{-4},10^{-3}\}{ 0 , 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT }.
We report results aggregated over 3 random seeds.
Table 12: Baseline results on GlobalWheat-wilds. In-distribution (ID) results correspond to the train-to-train setting. Parentheses show standard deviation across 3 replicates.
| | | | | |
| --- | --- | --- | --- | --- |
| Algorithm | Validation (ID) acc | Validation (OOD) acc | Test (ID) acc | Test (OOD) acc |
| ERM | 77.4 (1.1) | 68.6 (0.4) | 77.1 (0.5) | 51.2 (1.8) |
| Group DRO | 76.1 (1.0) | 66.2 (0.4) | 76.2 (0.8) | 47.9 (2.0) |
Table 13: Mixed-to-test comparison for ERM models on GlobalWheat-wilds.
In the official OOD setting, we train on data from Europe, whereas in the mixed-to-test ID setting, we train on a mix of data from Europe, Africa, and North America.
In both settings, we test on data from Africa and North America.
For this comparison, we report performance on 50% of the official test set (randomly selecting 50% of each test domain), with the rest of the test set mixed in to the training set in the mixed-to-test setting.
Parentheses show standard deviation across 3 replicates.
| | | |
| --- | --- | --- |
| Setting | Algorithm | Test accuracy (%) |
| Official (train on ID examples) | ERM | 49.6 (1.9) |
| Mixed-to-test (train on ID + OOD examples) | ERM | 63.3 (1.7) |
Table 14: Mixed-to-test comparison for ERM models on GlobalWheat-wilds, broken down by each test domain. This is a more detailed version of Table [13](#S5.T13 "Table 13 ‣ Model. ‣ E.5.2 Baseline results ‣ E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"). Parentheses show standard deviation across 3 replicates.
| | | | | | |
| --- | --- | --- | --- | --- | --- |
| Session | Country | # Images | ID (mixed-to-test) acc | OOD acc | ID-OOD gap |
| CIMMYT\_1 | Mexico | 35 | 63.1 (1.4) | 48.0 (2.6) | 15.1 |
| CIMMYT\_2 | Mexico | 39 | 76.1 (0.9) | 58.2 (3.6) | 17.9 |
| CIMMYT\_3 | Mexico | 30 | 65.6 (3.1) | 63.3 (2.1) | 2.3 |
| KSU\_1 | US | 50 | 73.5 (1.1) | 53.2 (2.3) | 20.3 |
| KSU\_2 | US | 50 | 73.6 (0.5) | 52.7 (2.7) | 20.9 |
| KSU\_3 | US | 48 | 73.3 (1.2) | 48.9 (3.0) | 24.4 |
| KSU\_4 | US | 30 | 68.3 (0.6) | 48.7 (3.5) | 19.6 |
| Terraref\_1 | US | 72 | 48.9 (0.5) | 17.9 (4.3) | 31.0 |
| Terraref\_2 | US | 53 | 34.7 (1.3) | 16.0 (3.4) | 18.7 |
| Usask\_1 | Canada | 100 | 78.3 (0.8) | 77.1 (1.4) | 1.2 |
| UQ\_1 | Australia | 11 | 41.8 (1.4) | 29.0 (1.0) | 12.8 |
| UQ\_2 | Australia | 8 | 81.6 (12.5) | 76.5 (14.4) | 5.1 |
| UQ\_3 | Australia | 7 | 56.4 (13.8) | 54.3 (10.0) | 2.1 |
| UQ\_4 | Australia | 15 | 68.8 (0.5) | 60.6 (1.3) | 8.2 |
| UQ\_5 | Australia | 15 | 54.4 (2.1) | 38.6 (2.1) | 15.8 |
| UQ\_6 | Australia | 15 | 75.8 (1.1) | 71.9 (0.7) | 3.9 |
| UQ\_7 | Australia | 9 | 68.9 (0.6) | 62.8 (2.5) | 6.1 |
| UQ\_8 | Australia | 21 | 58.6 (0.6) | 46.5 (2.1) | 11.1 |
| UQ\_9 | Australia | 17 | 54.7 (1.5) | 43.6 (2.1) | 11.1 |
| UQ\_10 | Australia | 53 | 61.7 (0.8) | 39.6 (2.5) | 22.1 |
| UQ\_11 | Australia | 42 | 50.4 (1.5) | 33.5 (2.7) | 16.9 |
| Total | | 720 | 63.3 (1.7) | 49.6 (1.9) | 13.7 |
##### ERM results and performance drops.
We ran both train-to-train and mixed-to-test comparisons.
For the train-to-train comparison, which uses the data splits described in the previous subsection, the Test (ID) accuracy is substantially higher than the Test (OOD) accuracy (77.1 (0.5) vs. 51.2 (1.8); Table [12](#S5.T12 "Table 12 ‣ Model. ‣ E.5.2 Baseline results ‣ E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). However, the Test (ID) and Test (OOD) sets come from entirely different regions, so this performance gap could also reflect a difference in the difficulty of the wheat head detection task in different regions (e.g., wheat heads that are more densely packed are harder to tell apart).
The mixed-to-test comparison controls for the test distribution by randomly splitting each test domain (acquisition session) into two halves, and then assigning one half to the training set. In other words, we randomly take out half of the test set and use it to replace existing examples in the training set, so that the total training set size is the same, and we retain the other half of the test set for evaluation.
We also evaluated the ERM model trained on the official split on this subsampled test set.
On this subsampled test set, the mixed-to-test ID accuracy is significantly higher than the OOD accuracy of the ERM model trained on the official split (63.3 (1.7) vs. 49.6 (1.9); Table [13](#S5.T13 "Table 13 ‣ Model. ‣ E.5.2 Baseline results ‣ E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
We also compared the per-domain accuracies of the models trained in the mixed-to-test and official settings (Table [14](#S5.T14 "Table 14 ‣ Model. ‣ E.5.2 Baseline results ‣ E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")) on the subsampled test set.
The accuracy drop is not evenly distributed across each domain, though some of the domains have a relatively small number of images, so there is some variance across random replicates.
The location/site of the acquisition session—which is correlated with factors like wheat genotype and the sensor used—has a large effect on performance (e.g., the KSU and Terraref sessions displayed a larger drop than the other sessions), but beyond that, it is not clear what factors are most strongly driving the accuracy drop.
The Terraref sessions were particularly difficult even in the mixed-to-test setting, because of the strong contrast in its photos and the presence of hidden wheat heads under leaves.
On the other hand, the KSU sessions had comparatively high accuracies in the mixed-to-test setting, but still displayed a large accuracy drop in the official OOD setting.
As the KSU sessions differed primarily in their development stages and had largely similar ID and OOD accuracies, development stage does not seem to be a main driver of the accuracy drop.
Finally, we note that the especially high variance across replicates for UQ\_2 and UQ\_3 is due to the proportion of empty images in those domains (88% for UQ\_2 and 57% for UQ\_3). Empty images are scored as either having 0% or 100% accuracy and therefore can have a large impact on the overall domain accuracy.
##### Additional baseline methods.
We also trained models with group DRO, treating each acquisition session as a domain, and using the same model hyperparameters as ERM.
However, the group DRO models perform poorly compared to the ERM model as reported in Table [12](#S5.T12 "Table 12 ‣ Model. ‣ E.5.2 Baseline results ‣ E.5 GlobalWheat-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
We leave the investigation of CORAL and IRM for future work because it is not straightforward to apply these algorithms to detection tasks.
##### Discussion.
Our baseline models were trained without any data augmentation, in contrast to baselines reported in the original dataset (David et al., [2020](#bib.bib104)).
Data augmentation could reduce the performance gap and warrants further investigation in future work, although David et al. ([2020](#bib.bib104)) still observed performance gaps on models trained with data augmentation in the original version of the dataset.
Moreover, while we evaluated models by their average performance across acquisition sessions, we noticed a large variability in performance across domains.
It is possible that some domains are more challenging or suffer from larger performance drops than others, and characterizing and mitigating these variations is interesting future work.
####
E.5.3 Broader context
Wheat head localization, while being an important operational trait for wheat breeders and farmers, is not the only deep learning application in plant phenotyping that suffers from lack of generalization. Other architectural traits such as plant segmentation (Sadeghi-Tehran et al., [2017](#bib.bib324); Kuznichov et al., [2019](#bib.bib217)), plant and plant organ detection (Fan et al., [2018](#bib.bib127); Madec et al., [2019](#bib.bib254)), leaves and organ disease classification (Fuentes et al., [2017](#bib.bib133); Shakoor et al., [2017](#bib.bib335); Toda and Okura, [2019](#bib.bib376)), and biomass and yield prediction (Aich et al., [2018](#bib.bib6); Dreccer et al., [2019](#bib.bib116)) would also benefit from plant phenotyping models that generalize to new deployments. In many of these applications, field images exhibit variations in illumination and sensors, and there has been work on mitigating biases across sensors (Ayalew et al., [2020](#bib.bib22); Gogoll et al., [2020](#bib.bib151)). Finally, developing models that generalize across plant species would benefit the breeding and growing of specialized crops that are presently under-represented in plant phenotyping research worldwide (Ward and Moghadam, [2020](#bib.bib396)).
We hope that GlobalWheat-wilds can foster the development of general solutions to plant phenotyping problems, increase collaboration between plant scientists and computer vision scientists, and encourage the development of new multi-domain plant datasets to ensure that plant phenotyping results are generalizable to all crop growing regions of the world.
####
E.5.4 Additional details
##### Modifications to the original dataset.
The data is taken directly from the 2021 Global Wheat Challenge (David et al., [2021](#bib.bib105)), which is an expanded version of the 2020 Global Wheat Challenge dataset (David et al., [2020](#bib.bib104)).
Compared to the challenge, the dataset splits are different:
we split off part of the training set to form the Validation (ID) and Test (ID) sets, and we rearranged the Validation (OOD) and Test (OOD) sets so that they split along disjoint continents.
Finally, we note that the 2021 challenge differs from the 2020 challenge in that images from North America were in the training set in the 2020 challenge, but were used for evaluation in the 2021 challenge, and are consequently assigned to the test set in GlobalWheat-wilds.
###
E.6 CivilComments-wilds
Automatic review of user-generated text is an important tool for moderating the sheer volume of text written on the Internet.
We focus here on the task of detecting toxic comments.
Prior work has shown that toxicity classifiers can pick up on biases in the training data and spuriously associate toxicity with the mention of certain demographics (Park et al., [2018](#bib.bib286); Dixon et al., [2018](#bib.bib112)).
These types of spurious correlations can significantly degrade model performance on particular subpopulations (Sagawa et al., [2020a](#bib.bib327)).
We study this issue through a modified variant of the CivilComments dataset (Borkan et al., [2019b](#bib.bib55)).
####
E.6.1 Setup
##### Problem setting.
We cast CivilComments-wilds as a subpopulation shift problem, where the subpopulations correspond to different demographic identities, and our goal is to do well on all subpopulations (and not just on average across these subpopulations).
Specifically, we focus on mitigating biases with respect to comments that mention particular demographic identities, and not comments written by members of those demographic identities; we discuss this distinction in the broader context section below.
The task is a binary classification task of determining if a comment is toxic.
Concretely, the input x𝑥xitalic\_x is a comment on an online article (comprising one or more sentences of text) and the label y𝑦yitalic\_y is whether it is rated toxic or not.
In CivilComments-wilds, unlike in most of the other datasets we consider, the domain annotation d𝑑ditalic\_d is a multi-dimensional binary vector, with the 8 dimensions corresponding to whether the comment mentions each of the 8 demographic identities male, female, LGBTQ, Christian, Muslim, other religions, Black, and White.
##### Data.
CivilComments-wilds comprises 450,000 comments, each annotated for toxicity and demographic mentions by multiple crowdworkers. We model toxicity classification as a binary task. Toxicity labels were obtained in the original dataset via crowdsourcing and majority vote, with each comment being reviewed by at least 10 crowdworkers. Annotations of demographic mentions were similarly obtained through crowdsourcing and majority vote.
Each comment was originally made on some online article. We randomly partitioned these articles into disjoint training, validation, and test splits, and then formed the corresponding datasets by taking all comments on the articles in those splits. This gives the following splits:
1. 1.
Training: 269,038 comments.
2. 2.
Validation: 45,180 comments.
3. 3.
Test: 133,782 comments.
##### Evaluation.
We evaluate a model by its worst-group accuracy, i.e., its lowest accuracy over groups of the test data that we define below.
As mentioned above, toxicity classifiers can spuriously latch onto mentions of particular demographic identities, resulting in a biased tendency to flag comments that innocuously mention certain demographic groups as toxic (Park et al., [2018](#bib.bib286); Dixon et al., [2018](#bib.bib112)).
To measure the extent of this bias, we define subpopulations based on whether they mention a particular demographic identity, compute the sensitivity (a.k.a. recall, or true positive rate) and specificity (a.k.a. true negative rate) of the classifier on each subpopulation,
and then report the worst of these two metrics over all subpopulations of interest.
This is equivalent to further dividing each subpopulation into two groups according to the label, and then computing the accuracy on each of these two groups.
Specifically, for each of the 8 identities we study (e.g., “male”), we form 2 groups based on the toxicity label
(e.g., one group of comments that mention the male gender and are toxic, and another group that mentions the male gender and are not toxic), for a total of 16 groups.
These groups overlap (a comment might mention multiple identities) and are not a complete partition (a comment might not mention any identity).
We then measure a model’s performance by its worst-group accuracy, i.e., its lowest accuracy over these 16 groups.
A high worst-group accuracy (relative to average accuracy) implies that the model is not spuriously associating a demographic identity with toxicity.
We can view this subpopulation shift problem as testing on multiple test distributions (corresponding to different subsets of the test set, based on demographic identities and the label) and reporting the worst performance over these different test distributions.
We use 16 groups (8 identities ×\times× 2 labels) instead of just 8 groups (8 identities) to capture the desire to balance true positive and true negative rates across each of the demographic identities.
Without splitting by the label, it would be possible for two different groups to have equal accuracies,
but one group might be much more likely to have non-toxic comments flagged as toxic, whereas the other group might be much more likely to have toxic comments flagged as non-toxic.
This would be undesirable from an application perspective, as such a model would still be biased against a particular demographic.
In Appendix [E.6.4](#S5.SS6.SSS4 "E.6.4 Additional details ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we further discuss the motivation for our choice of evaluation metric as well as its limitations.
As variability in performance over replicates can be high due to the small sizes of some demographic groups (Table [17](#S5.T17 "Table 17 ‣ Data processing. ‣ E.6.4 Additional details ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), we report results averaged over 5 random seeds, instead of the 3 seeds that we use for most other datasets.
##### Potential leverage.
Since demographic identity annotations are provided at training time, we have an i.i.d. dataset available at training time for each of the test distributions of interest (corresponding to each group).
Moreover, even though demographic identity annotations are unavailable at test time,
they are relatively straightforward to predict.
####
E.6.2 Baseline results
##### Model.
For all experiments, we fine-tuned DistilBERT-base-uncased models (Sanh et al., [2019](#bib.bib330)), using the implementation from Wolf et al. ([2019](#bib.bib405)) and with the following hyperparameter settings:
batch size 16; learning rate 10−5superscript10510^{-5}10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT using the AdamW optimizer (Loshchilov and Hutter, [2019](#bib.bib247)) for 5 epochs with early stopping; an L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strength of 10−2superscript10210^{-2}10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT;
and a maximum number of tokens of 300, since 99.95% of the input examples had ≤\leq≤300 tokens.
The learning rate was chosen through a grid search over
{10−6,2×10−6,10−5,2×10−5}superscript1062superscript106superscript1052superscript105\{10^{-6},2\times 10^{-6},10^{-5},2\times 10^{-5}\}{ 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 2 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 2 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT }, and all other hyperparameters were simply set to standard/default values.
##### ERM results and performance drops.
The ERM model does well on average, with 92.2% average accuracy (Table [15](#S5.T15 "Table 15 ‣ ERM results and performance drops. ‣ E.6.2 Baseline results ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). However, it does poorly on some subpopulations, e.g., with 57.4% accuracy on toxic comments that mention other religions.
Overall, accuracy on toxic comments (which are a minority of the dataset) was lower than accuracy on non-toxic comments, so we also trained a reweighted model that balanced toxic and non-toxic comments by upsampling the toxic comments. This reweighted model had a slightly worse average accuracy of 89.8% and a better worst-group accuracy of 69.2% (Table [15](#S5.T15 "Table 15 ‣ ERM results and performance drops. ‣ E.6.2 Baseline results ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), Reweighted (label)), but a significant gap remains between average and worst-group accuracies.
We note that the relatively small size of some of the demographic subpopulations makes it infeasible to run a test-to-test comparison, i.e., estimate how well a model could do on each subpopulation (corresponding to demographic identity) if it were trained on just that subpopulation.
For example, Black comments comprise only <4% of the training data,
and training just on those Black comments is insufficient to achieve high in-distribution accuracy.
Without running the test-to-test comparison, it is possible that the gap between average and worst-group accuracies can be explained at least in part by differences in the intrinsic difficulty of some of the subpopulations, e.g., the labels of some subpopulations might be noisier because human annotators might disagree more frequently on comments mentioning a particular demographic identity.
Future work will be required to establish estimates of in-distribution accuracies for each subpopulation that can account for these differences.
Table 15: Baseline results on CivilComments-wilds. The reweighted (label) algorithm samples equally from the positive and negative class; the group DRO (label) algorithm additionally weights these classes so as to minimize the maximum of the average positive training loss and average negative training loss.
Similarly, the reweighted (label ×\times× Black) and group DRO (label ×\times× Black) algorithms sample equally from the four groups corresponding to all combinations of class and whether there is a mention of Black identity. The CORAL and IRM algorithms extend the reweighted algorithm by adding their respective penalty terms, so they also sample equally from each group.
We show standard deviation across 5 random seeds in parentheses.
| | | | | |
| --- | --- | --- | --- | --- |
| Algorithm | Avg val acc | Worst-group val acc | Avg test acc | Worst-group test acc |
| ERM | 92.3 (0.2) | 50.5 (1.9) | 92.2 (0.1) | 56.0 (3.6) |
| Reweighted (label) | 90.1 (0.4) | 65.9 (1.8) | 89.8 (0.4) | 69.2 (0.9) |
| Group DRO (label) | 90.4 (0.4) | 65.0 (3.8) | 90.2 (0.3) | 69.1 (1.8) |
| Reweighted (label ×\times× Black) | 89.5 (0.6) | 66.6 (1.5) | 89.2 (0.6) | 66.2 (1.2) |
| CORAL (label ×\times× Black) | 88.9 (0.6) | 64.7 (1.4) | 88.7 (0.5) | 65.6 (1.3) |
| IRM (label ×\times× Black) | 89.0 (0.7) | 65.9 (2.8) | 88.8 (0.7) | 66.3 (2.1) |
| Group DRO (label ×\times× Black) | 90.1 (0.4) | 67.7 (1.8) | 89.9 (0.5) | 70.0 (2.0) |
Table 16: Accuracies on each subpopulation in CivilComments-wilds, averaged over models trained by group DRO (label).
| | | |
| --- | --- | --- |
| Demographic | Test accuracy on non-toxic comments | Test accuracy on toxic comments |
| Male | 88.4 (0.7) | 75.1 (2.1) |
| Female | 90.0 (0.6) | 73.7 (1.5) |
| LGBTQ | 76.0 (3.6) | 73.7 (4.0) |
| Christian | 92.6 (0.6) | 69.2 (2.0) |
| Muslim | 80.7 (1.9) | 72.1 (2.6) |
| Other religions | 87.4 (0.9) | 72.0 (2.5) |
| Black | 72.2 (2.3) | 79.6 (2.2) |
| White | 73.4 (1.4) | 78.8 (1.7) |
##### Additional baseline methods.
The CORAL, IRM, and group DRO baselines involve partitioning the training data into disjoint domains.
We study the following partitions, corresponding to different rows in Table [15](#S5.T15 "Table 15 ‣ ERM results and performance drops. ‣ E.6.2 Baseline results ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"):
1. 1.
Label: 2 domains, 1 for each class.
2. 2.
Label ×\times× Black: 4 domains, 1 for each combination of class and Black.
On the Label partition, we used Group DRO to train a model that seeks to balance the losses on the positive and negative examples. This performs similarly to the standard reweighted models described above
(Table [15](#S5.T15 "Table 15 ‣ ERM results and performance drops. ‣ E.6.2 Baseline results ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), Group DRO (label)).
We found that the worst-performing demographic for non-toxic comments was the Black demographic (Table [16](#S5.T16 "Table 16 ‣ ERM results and performance drops. ‣ E.6.2 Baseline results ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), which motivated the Label ×\times× Black partition. There, we used CORAL, IRM, and Group DRO to train models. However, these models did not perform significantly better (Table [15](#S5.T15 "Table 15 ‣ ERM results and performance drops. ‣ E.6.2 Baseline results ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), label ×\times× Black). While there were slight improvements on the Black groups, accuracy degraded on some other groups like non-toxic LBGTQ comments.
We note that our implementations of CORAL and IRM are built on top of the standard reweighting algorithm, i.e., they sample equally from each group. As these two algorithms perform similarly to
reweighting, it indicates that the additional penalty term is not significantly affecting performance.
Indeed, our grid search for the penalty weights selected the lowest value of the penalties (λ=10.0𝜆10.0\lambda=10.0italic\_λ = 10.0 for CORAL and λ=1.0𝜆1.0\lambda=1.0italic\_λ = 1.0 for IRM).
##### Discussion.
Adapting the baseline methods to handle multiple overlapping groups, which were not studied in their original settings, could be a potential approach to improving accuracy on this task.
Another potential approach is using baselining to account for different groups having different intrinsic levels of difficulty (Oren et al., [2019](#bib.bib281)).
For example, comments mentioning different demographic groups might differ in terms of how subjective classifying them is.
Others have also explored specialized data augmentation techniques for mitigating demographic biases in toxicity classifiers (Zhao et al., [2018](#bib.bib431)).
Adragna et al. ([2020](#bib.bib2)) recently used a simplified variant of the CivilComments dataset, with artificially-constructed training and test environments, to show a proof-of-concept that IRM can improve performance on minority groups. Methods such as IRM and group DRO rely heavily on the choice of groups/domains/environments; investigating the effect of different choices would be a useful direction for future work.
Other recent work has studied methods that try to automatically learn groups, for example, through unsupervised clustering (Oren et al., [2019](#bib.bib281); Sohoni et al., [2020](#bib.bib348))
or identifying high-loss points (Nam et al., [2020](#bib.bib270); Liu et al., [2021a](#bib.bib241)).
Toxicity classification is one application where human moderators can work together with an ML model to handle examples that the model is unsure about. However, Jones et al. ([2021](#bib.bib192)) found that using selective classifiers—where the model is allowed to abstain if it is unsure—can actually further worsen performance on minority subpopulations. This suggests that in addition to having low accuracy on minority subpopulations, standard models can be poorly calibrated on them.
Another important consideration for toxicity detection in practice is shifts over time, as online discourse changes quickly, and what is seen as toxic today might not have even appeared in the dataset from a few months ago. We do not study this distribution shift in this work. One limitation of the CivilComments-wilds dataset is that it is fixed to a relatively short period in time, with most comments being written in the span of a year; this makes it harder to use as a dataset for studying temporal shifts.
Finally, we note that collecting “ground truth” human annotation of toxicity is itself a subjective and challenging process; recent work has studied ways of making it less biased and more efficient (Sap et al., [2019](#bib.bib332); Han and Tsvetkov, [2020](#bib.bib162)).
####
E.6.3 Broader context
The CivilComments-wilds dataset does not assume that user demographics are available; instead, it uses mentions of different demographic identities in the actual comment text.
For example, we want models that do not associate comments that mention being Black with being toxic, regardless of whether a Black or non-Black person wrote the comment.
This setting is particularly relevant when user demographics are unavailable, e.g., when considering anonymous online comments.
A related and important setting is subpopulation shifts with respect to user demographics (e.g., the demographics of the author of the comment, regardless of the content of the comment).
Such demographic disparities have been widely documented in natural language and speech processing tasks (Hovy and Spruit, [2016](#bib.bib179)), among other areas.
For example, NLP models have been shown to obtain worse performance on African-American Vernacular English compared to Standard American English on
part-of-speech tagging (Jørgensen et al., [2015](#bib.bib195)),
dependency parsing (Blodgett et al., [2016](#bib.bib50)),
language identification (Blodgett and O’Connor, [2017](#bib.bib49)),
and auto-correct systems (Hashimoto et al., [2018](#bib.bib166)).
Similar disparities exist in speech, with state-of-the-art commercial systems obtaining higher word error rates on particular races (Koenecke et al., [2020](#bib.bib208)) and dialects (Tatman, [2017](#bib.bib366)).
These disparities are present not just in academic models, but in large-scale commercial systems that are already widely deployed, e.g., in speech-to-text systems from Amazon, Apple, Google, IBM, and Microsoft (Tatman, [2017](#bib.bib366); Koenecke et al., [2020](#bib.bib208)) or language identification systems from IBM, Microsoft, and Twitter (Blodgett and O’Connor, [2017](#bib.bib49)).
Indeed, the original CivilComments dataset was developed by Google’s Conversation AI team, which is also behind a public toxicity classifier (Perspective API) that was developed in partnership with The New York Times (NYTimes, [2016](#bib.bib279)).
####
E.6.4 Additional details
##### Evaluation metrics.
The evaluation metric used in the original competition was a complex weighted combination of various metrics, including subgroup AUCs for each demographic identity, and a new pinned AUC metric introduced by the original authors (Borkan et al., [2019b](#bib.bib55)); conceptually, these metrics also measure the degree to which model accuracy is uniform across the different identities.
After discussion with the original authors, we replace the composite metric with worst-group accuracy (i.e., worst TPR/FPR over identities) for simplicity.
Measuring subgroup AUCs can be misleading in this context, because it assumes that the classifier can set separate thresholds for different subgroups (Borkan et al., [2019b](#bib.bib55), [a](#bib.bib54)).
One downside is that measuring worst-group accuracy treats false positives and false negatives equally.
In deployment systems, one might want to weight these differently, e.g., using cost-sensitive learning or by simply raising or lowering the classification threshold,
especially since real data is highly imbalanced (with a lot more negatives than positives).
One could also binarize the labels and identities differently: in this benchmark, we simply use majority voting from the annotators.
Perhaps more fundamentally, even if TPR and FPR were balanced across different identities, this need not imply unambiguously equitable performance, because different subpopulations might have different intrinsic levels of noise and difficulty. See Corbett-Davies and Goel ([2018](#bib.bib92)) for more discussion of this problem of infra-marginality.
In practice, models might also do poorly on intersections of groups (Kearns et al., [2018](#bib.bib201)), e.g., on comments that mention multiple identities. Given the size of the dataset and comparative rarity of some identities and of toxic comments in general, accuracies on these intersections are difficult to estimate from this dataset.
A potential avenue of future work is to develop methods for evaluating models on such subgroups, e.g., by generating data in particular groups through templates
(Park et al., [2018](#bib.bib286); Ribeiro et al., [2020](#bib.bib314)).
##### Data processing.
The CivilComments-wilds dataset comprises comments from a large set of articles from the Civil Comments platform, annotated for toxicity and demographic identities (Borkan et al., [2019b](#bib.bib55)). We partitioned the articles into disjoint training, validation, and test splits, and then formed the corresponding datasets by taking all comments on the articles in those splits.
In total, the training set comprised 269,038 comments (60% of the data); the validation set comprised 45,180 comments (10%); and the test set comprised 133,782 (30%).
Table 17: Group sizes in the test data for CivilComments-wilds. The training and validation data follow similar proportions.
| | | |
| --- | --- | --- |
| Demographic | Number of non-toxic comments | Number of toxic comments |
| Male | 12092 | 2203 |
| Female | 14179 | 2270 |
| LGBTQ | 3210 | 1216 |
| Christian | 12101 | 1260 |
| Muslim | 5355 | 1627 |
| Other religions | 2980 | 520 |
| Black | 3335 | 1537 |
| White | 5723 | 2246 |
##### Modifications to the original dataset.
The original dataset888<www.kaggle.com/c/jigsaw-unintended-bias-in-toxicity-classification/> also had a training and test split with disjoint articles. These splits are related to ours in the following way. Let the number of articles in the original test split be m𝑚mitalic\_m. To form our validation split, we took m𝑚mitalic\_m articles (sampled uniformly at random) from the original training split, and to form our test split, we took 2m2𝑚2m2 italic\_m articles (also sampled uniformly at random) from the original training split and added it to the existing test split.
We added a fixed validation set to allow other researchers to be able to compare methods more consistently, and we tripled the size of the test set to allow for more accurate worst-group accuracy measurement.
Similarly, we combined some of the demographic identities in the original dataset to obtain larger groups (for which we could more accurately estimate accuracy). Specifically, we created an aggregate LGBTQ identity that combines the original
homosexual\_gay\_or\_lesbian,
bisexual,
other\_sexual\_orientation,
transgender, and
other\_gender identities (e.g., it is 1 if any of those identities are 1),
and an aggregate other\_religions identity that combines the original
jewish,
hindu,
buddhist,
atheist, and
other\_religion identities.
We also omitted the psychiatric\_or\_mental\_illness identity, which was evaluated in the original Kaggle competition, because of a lack of sufficient data for accurate estimation; but we note that baseline group accuracies for that identity seemed higher than for the other groups, so it is unlikely to factor into worst-group accuracy.
In our new split, each identity we evaluate on (male, female, LGBTQ, Christian, Muslim, other\_religions, Black, and White) has at least 500 positive and 500 negative examples.
In Table [17](#S5.T17 "Table 17 ‣ Data processing. ‣ E.6.4 Additional details ‣ E.6 CivilComments-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") we show the sizes of each subpopulation in the test set; the training and validation sets follow similar proportions.
For convenience, we also add an identity\_any identity; this combines all of the identities in the original dataset, including psychiatric\_or\_mental\_illness and related identities.
##### Additional baseline results.
We also trained a group DRO model using 29=512superscript295122^{9}=5122 start\_POSTSUPERSCRIPT 9 end\_POSTSUPERSCRIPT = 512 domains, 1 for each combination of class and the 8 identities. This model performed similarly to the other group DRO models.
##### Additional data sources.
All of the data, including the data with identity annotations that we use and the data with just label annotations, are also annotated for additional toxicity subtype attributes, specifically
severe\_toxicity,
obscene,
threat,
insult,
identity\_attack, and
sexual\_explicit.
These annotations can be used to train models that are more aware of the different ways that a comment can be toxic;
in particular, using the identity\_attack attribute to learn which comments are toxic because of the use of identities might help the model learn how to avoid spurious associations between toxicity and identity.
These additional annotations are included in the metadata provided through the Wilds package.
The original CivilComments dataset (Borkan et al., [2019b](#bib.bib55)) also contains ≈\approx≈1.5M training examples that have toxicity (label) annotations but not identity (group) annotations.
For simplicity, we have omitted these from the current version of CivilComments-wilds.
These additional data points can be downloaded from the original data source and could be used, for example, by first inferring which group each additional point belongs to, and then running group DRO or a similar algorithm that uses group annotations at training time.
###
E.7 FMoW-wilds
ML models for satellite imagery can enable global-scale monitoring of sustainability and economic challenges, aiding policy and humanitarian efforts in applications such as deforestation tracking (Hansen et al., [2013](#bib.bib164)), population density mapping (Tiecke et al., [2017](#bib.bib374)), crop yield prediction (Wang et al., [2020b](#bib.bib395)), and other economic tracking applications (Katona et al., [2018](#bib.bib199)).
As satellite data constantly changes due to human activity and environmental processes, these models must be robust to distribution shifts over time.
Moreover, as there can be disparities in the data available between regions,
these models should ideally have uniformly high accuracies instead of only doing well on data-rich regions and countries.
We study this problem on a variant of the Functional Map of the World dataset (Christie et al., [2018](#bib.bib83)).
####
E.7.1 Setup
##### Problem setting.
We consider a hybrid domain generalization and subpopulation shift problem, where the input x𝑥xitalic\_x is a RGB satellite image (resized to 224 ×\times× 224 pixels), the label y𝑦yitalic\_y is one of 62 building or land use categories, and the domain d𝑑ditalic\_d represents both the year the image was taken as well as its geographical region (Africa, the Americas, Oceania, Asia, or Europe).
We aim to solve both a domain generalization problem across time and improve subpopulation performance across regions.
##### Data.
FMoW-wilds is based on the Functional Map of the World dataset (Christie et al., [2018](#bib.bib83)), which collected and categorized high-resolution satellite images from over 200 countries based on the functional purpose of the buildings or land in the image, over the years 2002–2018 (see Figure [9](#S4.F9 "Figure 9 ‣ 4.3.1 FMoW-wilds: Land use classification across different regions and years ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
We use a subset of this data and split it into three time range domains, 2002–2013, 2013–2016, and 2016–2018, as well as five geographical regions as subpopulations (Africa, Americas, Oceania, Asia, and Europe).
For each example, we also provide the timestamp and location coordinates, though our baseline models only use the coarse time ranges and geographical regions instead of these additional metadata.
We use the following data splits:
1. 1.
Training: 76,863 images from the years 2002–2013.
2. 2.
Validation (OOD): 19,915 images from the years from 2013–2016.
3. 3.
Test (OOD): 22,108 images from the years from 2016–2018.
4. 4.
Validation (ID): 11,483 images from the years from 2002–2013.
5. 5.
Test (ID): 11,327 images from the years from 2002–2013.
The original dataset did not evaluate models under distribution shifts. Our training split is a subset of the original training dataset, filtered for images in the appropriate time range; similarly, our OOD and ID validation splits are subsets of the original validation dataset, and our OOD and ID test splits are subsets of the original test dataset. See Appendix [E.7.4](#S5.SS7.SSS4 "E.7.4 Additional details ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more dataset details.
The train/val/test data splits contain images from disjoint location coordinates, and all splits contain data from all 5 geographic regions.
The ID and OOD splits within the test and validation sets may have overlapping locations, but have non-overlapping time ranges.
There is a disparity in the number of examples in each region, with Africa and Oceania having the least examples (Figure [23](#S5.F23 "Figure 23 ‣ Data. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")); this could be due to bias in sampling and/or a lack of infrastructure and land data in certain regions.
Figure 23: Number of examples from each region of the world in FMoW-wilds on the ID vs. OOD splits of the data. There is much less data from Africa and Oceania than other regions.
##### Evaluation.
We evaluate models by their average and worst-region OOD accuracies. The former measures the ability of the model to generalize across time, while the latter additionally measures how well models do across different regions/subpopulations under a time shift.
Table 18: Average and worst-region accuracies (%) under time shifts in FMoW-wilds. Models are trained on data before 2013 and tested on held-out location coordinates from in-distribution (ID) or out-of-distribution (OOD) test sets.
ID results correspond to the train-to-train setting.
Parentheses show standard deviation across 3 replicates.
| | | | | |
| --- | --- | --- | --- | --- |
| | Validation (ID) | Validation (OOD) | Test (ID) | Test (OOD) |
| Average | | | | |
| ERM | 61.2 (0.52) | 59.5 (0.37) | 59.7 (0.65) | 53.0 (0.55) |
| CORAL | 58.3 (0.28) | 56.9 (0.25) | 57.2 (0.90) | 50.5 (0.36) |
| IRM | 58.6 (0.07) | 57.4 (0.37) | 57.7 (0.10) | 50.8 (0.13) |
| Group DRO | 60.5 (0.36) | 58.8 (0.19) | 59.4 (0.11) | 52.1 (0.50) |
| Worst-region | | | | |
| ERM | 59.2 (0.69) | 48.9 (0.62) | 58.3 (0.92) | 32.3 (1.25) |
| CORAL | 55.9 (0.50) | 47.1 (0.43) | 55.0 (1.02) | 31.7 (1.24) |
| IRM | 56.6 (0.59) | 47.5 (1.57) | 56.0 (0.34) | 30.0 (1.37) |
| Group DRO | 57.9 (0.62) | 46.5 (0.25) | 57.8 (0.60) | 30.8 (0.81) |
Table 19: The regional accuracies of models trained on data before 2013 and tested on held-out locations from ID (<2013absent2013<2013< 2013) or OOD (≥2016absent2016\geq 2016≥ 2016) test sets in FMoW-wilds. ID results correspond to the train-to-train setting. Standard deviations over 3 trials are in parentheses.
| | | | | | | |
| --- | --- | --- | --- | --- | --- | --- |
| | Asia | Europe | Africa | Americas | Oceania | Worst region |
| OOD Test | | | | | | |
| ERM | 55.4 (0.95) | 55.6 (0.53) | 32.3 (1.25) | 55.7 (0.48) | 59.1 (0.85) | 32.3 (1.25) |
| CORAL | 52.4 (0.96) | 52.6 (0.82) | 31.7 (1.24) | 53.3 (0.27) | 56.0 (2.02) | 31.7 (1.24) |
| IRM | 52.9 (0.73) | 53.9 (0.28) | 30.0 (1.37) | 53.7 (0.51) | 55.0 (2.22) | 30.0 (1.37) |
| Group DRO | 54.7 (0.52) | 55.1 (0.39) | 30.8 (0.81) | 54.6 (0.48) | 58.5 (1.65) | 30.8 (0.81) |
| ID Test | | | | | | |
| ERM | 58.9 (1.19) | 58.4 (0.81) | 69.1 (2.64) | 61.4 (0.35) | 69.9 (0.53) | 58.3 (0.92) |
| CORAL | 56.6 (1.35) | 55.0 (1.02) | 69.2 (2.92) | 59.7 (0.83) | 70.8 (2.53) | 55.0 (1.02) |
| IRM | 56.9 (0.62) | 56.0 (0.34) | 69.7 (2.16) | 59.7 (0.49) | 68.3 (2.00) | 56.0 (0.34) |
| Group DRO | 58.7 (0.33) | 57.9 (0.74) | 69.2 (0.28) | 61.1 (0.57) | 68.8 (2.38) | 57.8 (0.60) |
Table 20: Mixed-to-test comparison for ERM models on FMoW-wilds.
In the official setting, we train on ID examples (i.e., data from 2002–2013),
whereas in the mixed-to-test ID setting, we train on ID + OOD examples (i.e., the same amount of data but half from 2002–2013 and half from 2013–2018, using a held-out set of data from 2013–2018).
In both settings, we test on the same Test (ID) data (from 2002–2013) and Test (OOD) data (from 2013–2018) described in the official split.
Models trained on the official split degrade in performance under the time shift, especially on the last year (2017) of the test data, and also fare poorly on the subpopulation shift, with low worst-region accuracy.
Models trained on the mixed-to-test split have higher OOD average and last year accuracy and much higher OOD worst-region accuracy.
Standard deviations over 3 trials are in parentheses.
| | | | |
| --- | --- | --- | --- |
| | | Test (ID) | Test (OOD) |
| Setting | Algorithm | Average | Worst-region | Average | Last year | Worst-region |
| Official | ERM | 59.7 (0.65) | 58.3 (0.92) | 53.0 (0.55) | 48.1 (1.20) | 32.3 (1.25) |
| Mixed-to-test | ERM | 59.0 (0.47) | 56.9 (0.80) | 57.4 (0.27) | 54.3 (0.22) | 48.6 (0.89) |
##### Potential leverage.
FMoW-wilds considers both domain generalization across time and subpopulation shift across regions. As we provide both time and region annotations, models can leverage the structure across both space and time to improve robustness.
For example, one hypothesis is that infrastructure development occurs smoothly over time. Utilizing this gradual shift structure with the timestamp metadata may enable adaptation across longer time periods (Kumar et al., [2020](#bib.bib215)).
The data distribution may also shift smoothly over spatial locations, and so enforcing some consistency with respect to spatial structure may improve predictions (Rolf et al., [2020](#bib.bib319); Jean et al., [2018](#bib.bib188)).
Furthermore, to mitigate the fact that some regions (e.g., Africa) have less labeled data, one could potentially transfer knowledge of other regions with similar economies and infrastructure. The location coordinate metadata allows for transfer learning across similar locations at any spatial scale.
####
E.7.2 Baseline results
##### Model.
For all experiments, we follow Christie et al. ([2018](#bib.bib83)) and use a DenseNet-121 model (Huang et al., [2017](#bib.bib183)) pretrained on ImageNet and with no L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT regularization.
We use the Adam optimizer (Kingma and Ba, [2015](#bib.bib207)) with an initial learning rate of 10−4superscript10410^{-4}10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT that decays by 0.96 per epoch, and train for 50 epochs for with early stopping and with a batch size of 64.
All reported results are averaged over 3 random seeds.
##### ERM results and performance drops.
In the train-to-train comparison, Table [20](#S5.T20 "Table 20 ‣ Evaluation. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that average accuracy drops by 6.7% when evaluated on the OOD test set (≥2016absent2016\geq 2016≥ 2016) compared to the ID test set setting.
The drop in average accuracy is especially large (11.6%) on images from the last year of the dataset (2017), furthest in the future from the training set.
In addition, there is a substantial 26.0% drop in worst-region accuracy, with the model performing much worse in Africa than other regions (Table [19](#S5.T19 "Table 19 ‣ Evaluation. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
We also ran a mixed-to-test comparison where we mixed in some data from the OOD period (2013–2018) into the training set, while keeping the overall training set size constant.
A model trained on this mixed split had a much smaller drop in performance under the time and region shifts (Table [20](#S5.T20 "Table 20 ‣ Evaluation. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
While the magnitude of the ID-OOD gap in worst-region accuracy shrinks from 26.0% in the train-to-train setting to 16.3% in the mixed-to-test setting, the gap remains significant, implying that the drop in performance is largely due to the distribution shift across time and region instead of a change in the intrinsic difficulty of the OOD data.
##### Additional baseline methods.
We compare ERM against CORAL, IRM, and Group DRO, using examples from different years as distinct domains. Table [18](#S5.T18 "Table 18 ‣ Evaluation. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that many of these methods are comparable or worse than ERM in terms of both ID and OOD test performance.
As with most other datasets, our grid search selected the lowest values of the penalty weights for CORAL (λ=0.1𝜆0.1\lambda=0.1italic\_λ = 0.1) and IRM (λ=1𝜆1\lambda=1italic\_λ = 1).
##### Discussion.
Intriguingly, a large subpopulation shift across regions only occurs with a combination of time and region shift.
This is corroborated by the mixed-split region shift results (Table [20](#S5.T20 "Table 20 ‣ Evaluation. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), which do not have a time shift between training and test sets, and correspondingly do not display a large disparity in performance across regions.
This drop in performance may be partially due to label shift:
from Figure [24](#S5.F24 "Figure 24 ‣ Discussion. ‣ E.7.2 Baseline results ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we see that the label distributions between Africa and other regions are very different, e.g., with a large drop in recreational facilities and a sharp increase in single residential units.
We do not find a similarly large label shift between <2013absent2013<2013< 2013 and ≥2013absent2013\geq 2013≥ 2013 splits of the dataset.
Figure 24: Number of examples from each category in FMoW-wilds in non-African and African regions. There is a large label shift between non-African regions and Africa.
Despite having the smallest number of training examples (Figure [23](#S5.F23 "Figure 23 ‣ Data. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), the baseline models do not suffer a drop in performance in Oceania on validation or test sets (Table [19](#S5.T19 "Table 19 ‣ Evaluation. ‣ E.7.1 Setup ‣ E.7 FMoW-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). We hypothesize that infrastructure in Oceania is more similar to regions with a large amount of data than Africa.
In contrast, Africa may be more distinct and may have changed more drastically over 2002-2018, the time extent of the dataset.
This suggests that the subpopulation shift is not merely a function of the number of training examples.
We note that our dataset splits can separate on particular factors such as the introduction of new sensors, which is natural with progression over time. For example, the WorldView-3 sensor came online in 2014. Future work should look into the role of auxiliary factors such as new sensors that are associated with time but may be controllable. We did not find a sharp difference in performance due to the introduction of WorldView-3; we found that the performance decays gradually over time, suggesting that the performance drop comes from other factors.
As with PovertyMap-wilds, there are important ethical considerations associated with remote sensing applications,
e.g., around surveillance and privacy issues, as well as the potential for systematic biases that negatively affect particular populations.
As an example of the latter, the poor model performance on satellite images from Africa that we observe in FMoW-wilds raises issues of bias and fairness.
With regard to privacy, we note that the image resolution in FMoW-wilds is lower than that of other public and easily-accessible satellite data such as that from Google Maps.
We refer interested readers to the UNICEF discussion paper by Berman et al. ([2018](#bib.bib45)) for a more in-depth discussion of the ethics of remote sensing especially as it pertains to development and humanitarian endeavors.
####
E.7.3 Broader context
Recognizing infrastructure and land features is crucial to many remote sensing applications. For example, in crop land prediction Wang et al. ([2020b](#bib.bib395)), recognizing gridded plot lines, plot circles, farm houses, and other visible features are important in recognizing crop fields. However, farming practices and equipment evolve over time and vary widely across the world, requiring both robust object recognition and synthesis of their different usage patterns.
Although the data is typically limited, we desire generalization on a global scale without requiring frequent large-scale efforts to gather more ground-truth data.
It is natural to have labeled data with limited temporal or spatial extent since ground truth generally must be verified on the ground or requires manual annotations from domain experts (i.e., they are often hard to be crowdsourced). A number of existing remote sensing datasets have limited spatial or temporal scope, including the UC Merced Land Use Dataset (Yang and Newsam, [2010](#bib.bib419)), TorontoCity (Wang et al., [2017](#bib.bib394)), and SpaceNet (DigitalGlobe and Works, [2016](#bib.bib110)).
However, works based on these datasets generally do not systematically study shifts in time or location.
####
E.7.4 Additional details
##### Data processing and modifications to the original dataset.
The FMoW-wilds dataset is derived from Christie et al. ([2018](#bib.bib83)), which collected over 1 million satellite images from over 200 countries over 2002-2018.
We use the RGB version of the original dataset, which contains 523,846 total examples, excluding the multispectral version of the images.
Methods that can utilize a sequence of images can group the images from the same location across multiple years together as input, but we consider the simple formulation here for our baseline evaluation.
The original dataset from Christie et al. ([2018](#bib.bib83)) is provided as a set of hierarchical directories with JPEG images of varying sizes.
To reduce download times and I/O usage, we resize these images to 224 ×\times× 224 pixels, and then store them as PNG images.
We also collect all the metadata into CSV format for easy processing.
The original dataset is posed as a image time-series classification problem, where the model has access to a sequence of images at each location. For simplicity, we treat each image as a separate example, while making sure that the data splits all contain disjoint locations. We use the train/val/test splits from the original dataset, but separate out two OOD time segments: we treat the original validation data from 2013-2016 as OOD val and the original test data from 2016-2018 as OOD test. We remove data from after 2013 from the training set, which reduces the size of the training set in comparison to the original dataset.
##### Additional challenges in high-resolution satellite datasets.
Compared to PovertyMap-wilds, FMoW-wilds contains much higher resolution images (sub-meter resolution vs. 30m resolution) and contains a larger variety of viewpoints/tilts, both of which could present computational or algorithmic challenges. For computational purposes, we resized all images to 224×224224224224\times 224224 × 224 (following Christie et al. ([2018](#bib.bib83))), but raw images can be thousands of pixels wide. Some recent works have tried to balance this tradeoff between viewing overall context and the fine-grained detail (Uzkent and Ermon, [2020](#bib.bib382); Kim et al., [2016a](#bib.bib204)), but how best to do this is an open question. FMoW-wilds also contains additional information on azimuth and cloud cover which could be used to correct for the variety in viewpoints and image quality.
###
E.8 PovertyMap-wilds
A different application of satellite imagery is poverty estimation across different spatial regions, which is essential for targeted humanitarian efforts in poor regions (Abelson et al., [2014](#bib.bib1); Espey et al., [2015](#bib.bib124)).
However, ground-truth measurements of poverty are lacking for much of the developing world, as field surveys are expensive (Blumenstock et al., [2015](#bib.bib51); Xie et al., [2016](#bib.bib415); Jean et al., [2016](#bib.bib187)).
For example, at least 4 years pass between nationally representative consumption or asset wealth surveys in the majority of African countries, with seven countries that had either never conducted a survey or had gaps of over a decade between surveys (Yeh et al., [2020](#bib.bib422)).
One approach to this problem is to train ML models on countries with ground truth labels and then deploy them to different countries where we have satellite data but no labels.
We study this problem through a variant of the poverty mapping dataset collected by Yeh et al. ([2020](#bib.bib422)).
####
E.8.1 Setup
##### Problem setting.
We consider a hybrid domain generalization and subpopulation shift problem,
where the input x𝑥xitalic\_x is a multispectral LandSat satellite image with 8 channels (resized to 224 ×\times× 224 pixels),
the output y𝑦yitalic\_y is a real-valued asset wealth index computed from Demographic and Health Surveys (DHS) data, and the domain d𝑑ditalic\_d represents the country the image was taken in and whether the image is of an urban or rural area.
We aim to solve both a domain generalization problem across country borders and improve subpopulation performance across urban and rural areas.
##### Data.
PovertyMap-wilds is based on a dataset collected by Yeh et al. ([2020](#bib.bib422)), which assembles satellite imagery and survey data at 19,669 villages from 23 African countries between 2009 and 2016 (Figure [10](#S4.F10 "Figure 10 ‣ 4.3.2 PovertyMap-wilds: Poverty mapping across different countries ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
Each input image has 8 channels: 7 from the LandSat satellite and an 8th channel for nighttime light intensity from a separate satellite,
as prior work has established that these night lights correlate with poverty measures (Noor et al., [2008](#bib.bib276); Elvidge et al., [2009](#bib.bib122)).
There are 23×2=462324623\times 2=4623 × 2 = 46 domains corresponding to the 23 countries and whether the location is urban or rural.
Each example comes with metadata on its location coordinates, survey year, and its urban/rural classification.
In contrast to other datasets, which have a single fixed ID/OOD split, the relatively small size of PovertyMap-wilds allows us to use 5 different folds, where each fold defines a different set of OOD countries.
In each fold, we use the following splits of the data (the number of countries and images in each split varies slightly from fold to fold):
1. 1.
Training: ∼similar-to\sim∼10000 images from 13–14 countries.
2. 2.
Validation (OOD): ∼similar-to\sim∼4000 images from 4–5 different countries (distinct from training and test (OOD) countries).
3. 3.
Test (OOD): ∼similar-to\sim∼4000 images from 4–5 different countries (distinct from training and validation (OOD) countries).
4. 4.
Validation (ID): ∼similar-to\sim∼1000 images from the same 13–14 countries in the training set.
5. 5.
Test (ID): ∼similar-to\sim∼1000 images from the same 13–14 countries in the training set.
All splits contain images of both urban and rural locations, with the countries assigned randomly to each split in each fold.
The distribution of wealth may shift across countries due to differing levels economic development, agricultural practices, and other factors. For example, Abelson et al. ([2014](#bib.bib1)) use thatched vs. metal roofs to distinguish between poor and wealthy households, respectively in Kenya and Uganda. However, other countries may have a different mapping of roof type to wealth where metal roofs signify more poor households. Similar issues can arise when looking at the health of crops (related to vegetation indices such as NDVI that are simple functions of the multispectral channels in the satellite image) as a sign for wealth in rural areas, since crop health is related to climate and the choice of crops, which vary upon region.
Asset wealth may also shift dramatically between countries. Figure [25](#S5.F25 "Figure 25 ‣ Data. ‣ E.8.1 Setup ‣ E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows the mean asset wealth per country, as well as urban vs. rural asset wealth per country.
Mean asset wealth ranges from -0.4 to +0.8 depending on the country.
There is a stark difference between mean asset wealth in urban and rural areas, with urban asset wealth being positive in all countries while rural mean asset wealth being mostly negative.
Figure 25: Mean asset wealth by country on aggregate as well as urban and rural splits for each country, computed on the full dataset.
##### Evaluation.
As is standard in the literature (Jean et al., [2016](#bib.bib187); Yeh et al., [2020](#bib.bib422)), the models are evaluated on the Pearson correlation (r𝑟ritalic\_r) between their predicted and actual asset wealth indices.
We measure the average correlation, to test generalization under country shifts, and also the lower of the correlations on the urban and rural subpopulations, to test generalization between urban and rural subpopulations.
We report the latter as previous works on poverty prediction from satellite imagery have noted that a significant part of model performance relies on distinguishing urban vs. rural areas, and improving performance within these subpopulations is an ongoing challenge, with rural areas generally faring worse under existing models (Jean et al., [2016](#bib.bib187); Yeh et al., [2020](#bib.bib422)).
We average all correlations across the 5 different folds, using 1 random seed per fold. The resulting standard deviations reflect the fact that different folds have different levels of difficulty (e.g., depending on how similar the ID and OOD countries are).
For the purposes of comparing different algorithms and models, we note that these standard deviations might make the comparisons appear noisier than they are, since a model might perform similarly across random seeds but still have a high standard deviation if it has different performances on different folds on the data.
In contrast, other Wilds datasets report results on the same data split but averaged across different random seeds.
##### Potential leverage.
Large socioeconomic differences between countries makes generalization across borders challenging. However, some indicators of wealth are known to be robust and are able to be seen from space. For example, roof type (e.g. thatched or metal roofing) has been shown to be a reliable proxy for wealth (Abelson et al., [2014](#bib.bib1)), and contextual factors such as the health of nearby croplands, the presence of paved roads, and connections to urban areas are plausibly reliable signals for measuring poverty.
Poverty measures are also known to be highly correlated across space, meaning nearby villages will likely have similar poverty measures, and methods can utilize this spatial structure (using the provided location coordinate metadata) to improve predictions (Jean et al., [2018](#bib.bib188); Rolf et al., [2020](#bib.bib319)).
We show the correlation with distance in Figure [26](#S5.F26 "Figure 26 ‣ Potential leverage. ‣ E.8.1 Setup ‣ E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), which plots the distance between pairs of data points against the absolute differences in asset wealth between pairs.
Figure 26: Mean absolute difference in asset wealth between two data points in the full dataset as a function of (great circle) distance between the two points. Smaller distances between data points correlate with more similar asset wealth measures. The pairs are binned by distance on a log (base 10) scale (100 bins), and the mean value of each bin is plotted at the midpoint distance of each bin.
####
E.8.2 Baseline results
##### Model.
For all experiments, we follow Yeh et al. ([2020](#bib.bib422)) and train a ResNet-18 model (He et al., [2016](#bib.bib167)) to minimize squared error.
We use the Adam optimizer (Kingma and Ba, [2015](#bib.bib207)) with an initial learning rate of 10−3superscript10310^{-3}10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT that decays by 0.96 per epoch, and train for 200 epochs for with early stopping (on OOD r𝑟ritalic\_r) and with a batch size of 64.
##### ERM results and performance drops.
When shifting across country borders, Table [21](#S5.T21 "Table 21 ‣ ERM results and performance drops. ‣ E.8.2 Baseline results ‣ E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that ERM suffers a 0.04 drop in average r𝑟ritalic\_r in the official OOD setting compared to the train-to-train ID setting.
Moreover, the drop in performance is exacerbated when looking at urban and rural subpopulations, even though all splits contain urban and rural examples;
the difference in worst r𝑟ritalic\_r over the urban and rural subpopulations triples from 0.04 to 0.12 compared to the difference in average r𝑟ritalic\_r.
Correlation is consistently lower on the rural subpopulation than the urban subpopulation.
We ran an additional mixed-to-test comparison where we considered an alternative training set with data that was uniformly sampled from all countries, while keeping the overall training set size constant (i.e., compared to the standard training set, it has fewer examples from each country, but data from more countries).
A model trained on this mixed split had a much smaller drop in performance between the ID and OOD test sets (Table [22](#S5.T22 "Table 22 ‣ ERM results and performance drops. ‣ E.8.2 Baseline results ‣ E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), which implies that the performance drop between the ID and OOD test sets is largely due to the distribution shift from seen to unseen countries.
Table 21: Pearson correlation r𝑟ritalic\_r (higher is better) on in-distribution and out-of-distribution (unseen countries) held-out sets in PovertyMap-wilds, including results on the rural subpopulations.
ID results correspond to the train-to-train setting.
All results are averaged over 5 different OOD country folds taken from Yeh et al. ([2020](#bib.bib422)), with standard deviations across different folds in parentheses.
| | | | | |
| --- | --- | --- | --- | --- |
| | Validation (ID) | Validation (OOD) | Test (ID) | Test (OOD) |
| Overall | | | | |
| ERM | 0.82 (0.02) | 0.80 (0.04) | 0.82 (0.03) | 0.78 (0.04) |
| CORAL | 0.82 (0.00) | 0.80 (0.04) | 0.83 (0.01) | 0.78 (0.05) |
| IRM | 0.82 (0.02) | 0.81 (0.03) | 0.82 (0.02) | 0.77 (0.05) |
| Group DRO | 0.78 (0.03) | 0.78 (0.05) | 0.80 (0.03) | 0.75 (0.07) |
| Worst urban/rural subpop | | | | |
| ERM | 0.58 (0.07) | 0.51 (0.06) | 0.57 (0.07) | 0.45 (0.06) |
| CORAL | 0.59 (0.04) | 0.52 (0.06) | 0.59 (0.03) | 0.44 (0.06) |
| IRM | 0.57 (0.06) | 0.53 (0.05) | 0.57 (0.08) | 0.43 (0.07) |
| Group DRO | 0.49 (0.08) | 0.46 (0.04) | 0.54 (0.11) | 0.39 (0.06) |
Table 22: Mixed-to-test comparison for ERM models on PovertyMap-wilds.
In the official OOD setting, we train on data from one set of countries, and then test on a different set of countries.
In the mixed-to-test setting, we train on the same amount of data but sampled uniformly from all countries, and then test on data from the same countries as in the official setting.
The Test (ID) and Test (OOD) sets used for the mixed-to-test results are smaller (subsampled at random) than those used for the official results, as some test examples were used for the training set in the mixed-to-test setting.
Models trained on the official split degrade in performance, especially on rural subpopulations,
while models trained on the mixed-to-test split do not.
| | | |
| --- | --- | --- |
| | Test (ID) | Test (OOD) |
| Setting | Overall r𝑟ritalic\_r | Rural r𝑟ritalic\_r | Urban r𝑟ritalic\_r | Overall r𝑟ritalic\_r | Rural r𝑟ritalic\_r | Urban r𝑟ritalic\_r |
| Official | 0.82 (0.03) | 0.57 (0.07) | 0.66 (0.04) | 0.78 (0.04) | 0.46 (0.05) | 0.59 (0.11) |
| Mixed-to-test | 0.83 (0.02) | 0.61 (0.08) | 0.65 (0.06) | 0.83 (0.03) | 0.60 (0.06) | 0.65 (0.06) |
##### Additional baseline methods.
We trained models with CORAL, IRM, and Group DRO, taking examples from different countries as coming from distinct domains.
Table [21](#S5.T21 "Table 21 ‣ ERM results and performance drops. ‣ E.8.2 Baseline results ‣ E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that these baselines are generally comparable to ERM and that they continue to be susceptible to shifts across countries and urban/rural areas.
As with most other datasets, our grid search selected the lowest values of the penalty weights for CORAL (λ=0.1𝜆0.1\lambda=0.1italic\_λ = 0.1) and IRM (λ=1𝜆1\lambda=1italic\_λ = 1).
##### Discussion.
These results corroborate performance drops seen in previous out-of-country generalization tests for poverty prediction from satellite imagery (Jean et al., [2016](#bib.bib187)).
In general, differences in infrastructure, economic development, agricultural practices, and even cultural differences can cause large shifts across country borders.
Differences between urban and rural subpopulations have also been well-documented (Jean et al., [2016](#bib.bib187); Yeh et al., [2020](#bib.bib422)). Models based on nighttime light information could suffer more in rural areas where nighttime light intensity is uniformly low or even zero.
Since survey years are also available, we could also investigate the robustness of the model over time. This would enable the models to be used for a longer time before needing more updated survey data, and we leave this to future work. Yeh et al. ([2020](#bib.bib422)) investigated predicting the change in asset wealth for individual villages in the World Bank Living Standards Measurement Surveys (LSMS), which is a longitudinal study containing multiple samples from the same village.
PovertyMap-wilds only contains cross-sectional samples which do not provide direct supervision for changes over time at any one location, but it is still possible to consider aggregate shifts across years.
As with FMoW-wilds, there are important ethical considerations associated with remote sensing applications,
e.g., around surveillance and privacy issues, as well as the potential for systematic biases that negatively affect particular populations.
As we describe in Section [E.8.4](#S5.SS8.SSS4 "E.8.4 Additional details ‣ E.8 PovertyMap-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), noise has been added to the location metadata in PovertyMap-wilds to protect privacy.
The distribution shifts across country and urban/rural boundaries that we study in PovertyMap-wilds are an example of a bias that affects model performance and therefore could have adverse policy consequences.
We refer interested readers to the UNICEF discussion paper by Berman et al. ([2018](#bib.bib45)) for a more in-depth discussion of the ethics of remote sensing especially as it pertains to development and humanitarian endeavors.
####
E.8.3 Broader context
Computational sustainability applications in the developing world also include tracking child mortality (Burke et al., [2016](#bib.bib68); Osgood-Zimmerman et al., [2018](#bib.bib282); Reiner et al., [2018](#bib.bib310)), educational attainment (Graetz et al., [2018](#bib.bib154)), and
food security and crop yield prediction (You et al., [2017](#bib.bib423); Wang et al., [2020b](#bib.bib395); Xie et al., [2020](#bib.bib416)).
Remote sensing data and satellite imagery has the potential to enable high-resolution maps of many of these sustainability challenges, but as with poverty measures, ground truth labels in these applications come from expensive surveys or observations from human workers in the field.
Some prior works consider using spatial structure (Jean et al., [2018](#bib.bib188); Rolf et al., [2020](#bib.bib319)), unlabeled data (Xie et al., [2016](#bib.bib415); Jean et al., [2018](#bib.bib188); Xie et al., [2020](#bib.bib416)), or weak sources of supervision (Wang et al., [2020b](#bib.bib395)) to improve global models despite the lack of ground-truth data.
We hope that PovertyMap-wilds can be used to improve the robustness of machine learning techniques on satellite data, providing an avenue for cheaper and faster measurements that can be used to make progress on a general set of computational sustainability challenges.
####
E.8.4 Additional details
##### Data processing.
The PovertyMap-wilds dataset is derived from Yeh et al. ([2020](#bib.bib422)), which gathers LandSat imagery and Demographic and Health Surveys (DHS) data from 19669 villages across 23 countries in Africa .
The images are 224×224224224224\times 224224 × 224 pixels large over 7 multispectral channels and an eighth nighttime light intensity channel. The LandSat satellite has a 30m resolution, meaning that each pixel of the image covers a 30m230superscript𝑚230m^{2}30 italic\_m start\_POSTSUPERSCRIPT 2 end\_POSTSUPERSCRIPT spatial area.
The location metadata is perturbed by the DHS as a privacy protection scheme; urban locations are randomly displaced by up to 2km and rural locations are perturbed by up to 10km. While this adds noise to the data, having a large enough image can guarantee that the location is in the image most of the time.
The target is a real-valued composite asset wealth index computed as the first principal component of survey responses about household assets, which is thought to be a less noisy measure of households’ longer-run economic well-being than other welfare measurements like consumption expenditure (Sahn and Stifel, [2003](#bib.bib329); Filmer and Scott, [2011](#bib.bib130)).
Asset wealth also has the advantage of not requiring adjustments for inflation or for purchasing power parity (PPP), as it is not based on a currency.
We normalize each channel by the pixel-wise mean and standard deviation for each channel, following (Yeh et al., [2020](#bib.bib422)). We also do a similar data augmentation scheme, adding random horizontal and vertical flips as well as color jitter (brightness factor 0.8, contrast factor 0.8, saturation factor 0.8, hue factor 0.1).
The data download process provided by Yeh et al. ([2020](#bib.bib422)) involves downloading and processing imagery from Google Earth Engine. We process each image into a compressed NumPy array with 8 channels. We also provide all the metadata in a CSV format.
##### Additional results.
We also ran an ablation where we removed the nighttime light intensity channel.
This resulted in a drop in OOD r𝑟ritalic\_r of 0.04 on average and 0.06 on the rural subpopulation, demonstrating the usefulness of the nightlight data in asset wealth estimation.
##### Modifications to the original dataset.
We report a much larger drop in correlation due to spatial shift than in Yeh et al. ([2020](#bib.bib422)).
To explain this, we note that our data splitting method is slightly different from theirs.
They have two separate experiments (with different data splits) to test in-distribution vs. out-of-distribution generalization.
In contrast, our data splits on both held-out in-distribution and out-of-distribution points at the same time with respect to the same training set, thus allowing us to compare both metrics simultaneously on one model as a more direct comparison.
We use the same OOD country folds as the original dataset.
However, Yeh et al. ([2020](#bib.bib422)) split the ID train/val/test while making sure that the spatial extent of the images between each split never overlap,
while we simply take uniformly random splits of the ID data.
This means that between our ID train/val/test splits, we may have images that have share some overlapping spatial extent, for example for two very nearby locations.
Thus, a model can utilize some memorization here to improve ID performance.
We believe this is reasonable since, with more ID data, more of the spatial area will be labeled and memorization should become an increasingly viable strategy for generalization in-domain.
###
E.9 Amazon-wilds
In many consumer-facing ML applications, models are trained on data collected on one set of users and then deployed across a wide range of potentially new users. These models can perform well on average but poorly on some individuals (Tatman, [2017](#bib.bib366); Caldas et al., [2018](#bib.bib72); Li et al., [2019b](#bib.bib235); Koenecke et al., [2020](#bib.bib208)).
These large performance disparities across users are practical concerns in consumer-facing applications, and they can also indicate that models are exploiting biases or spurious correlations in the data (Badgeley et al., [2019](#bib.bib24); Geva et al., [2019](#bib.bib146)).
We study this issue of inter-individual performance disparities on a variant of the Amazon-wilds Reviews dataset (Ni et al., [2019](#bib.bib274)).
####
E.9.1 Setup
##### Problem setting.
We consider a hybrid domain generalization and subpopulation problem where the domains correspond to different reviewers.
The task is multi-class sentiment classification, where the input x𝑥xitalic\_x is the text of a review, the label y𝑦yitalic\_y is a corresponding star rating from 1 to 5, and the domain d𝑑ditalic\_d is the identifier of the reviewer who wrote the review.
Our goal is to perform consistently well across a wide range of reviewers, i.e., to achieve high tail performance on different subpopulations of reviewers in addition to high average performance. In addition, we consider disjoint set of reviewers between training and test time.
##### Data.
The dataset comprises 539,502 customer reviews on Amazon taken from the Amazon Reviews dataset (Ni et al., [2019](#bib.bib274)).
Each input example has a maximum token length of 512.
For each example, the following additional metadata is also available at both training and evaluation time: reviewer ID, product ID, product category, review time, and summary.
To reliably measure model performance on each reviewer, we include at least 75 reviews per reviewer in each split.
Concretely, we consider the following splits, where reviewers are randomly assigned to either in-distribution or out-of-distribution sets:
1. 1.
Training: 245,502 reviews from 1,252 reviewers.
2. 2.
Validation (OOD): 100,050 reviews from another set of 1,334 reviewers, distinct from training and test (OOD).
3. 3.
Test (OOD): 100,050 reviews from another set of 1,334 reviewers, distinct from training and validation (OOD).
4. 4.
Validation (ID): 46,950 reviews from 626 of the 1,252 reviewers in the training set.
5. 5.
Test (ID): 46,950 reviews from 626 of the 1,252 reviewers in the training set.
The reviewers in the train and in-distribution splits; the validation (OOD) split; and the test (OOD) split are all disjoint,
which allows us to test generalization to unseen reviewers.
See Appendix [E.9.4](#S5.SS9.SSS4 "E.9.4 Additional details ‣ E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") for more details.
##### Evaluation.
To assess whether models perform consistently well across reviewers, we evaluate models by their accuracy on the reviewer at the 10th percentile.
This follows the federated learning literature, where it is standard to measure model performance on devices and users at various percentiles in an effort to encourage good performance across many devices (Caldas et al., [2018](#bib.bib72); Li et al., [2019b](#bib.bib235)).
##### Potential leverage.
We include more than a thousand reviewers in the training set, capturing variation across a wide range of reviewers.
In addition, we provide reviewer ID annotations for all reviews in the dataset.
These annotations could be used to directly mitigate performance disparities across reviewers seen during training time.
####
E.9.2 Baseline results
Table 23: Baseline results on Amazon-wilds. We report the accuracy of models trained using ERM, CORAL, IRM, and group DRO, as well as a reweighting baseline that reweights for class balance. To measure tail performance across reviewers, we report the accuracy for the reviewer in the 10th percentile. While the performance drop on Amazon-wilds is primarily from subpopulation shift, there is also a performance drop from evaluating on unseen reviewers, as evident in the gaps in accuracies between the in-distribution and the out-of-distribution sets.
Validation (ID)
Validation (OOD)
Test (ID)
Test (OOD)
Algorithm
10th percentile
Average
10th percentile
Average
10th percentile
Average
10th percentile
Average
ERM
58.7 (0.0)
75.7 (0.2)
55.2 (0.7)
72.7 (0.1)
57.3 (0.0)
74.7 (0.1)
53.8 (0.8)
71.9 (0.1)
CORAL
56.2 (1.7)
74.4 (0.3)
54.7 (0.0)
72.0 (0.3)
55.1 (0.4)
73.4 (0.2)
52.9 (0.8)
71.1 (0.3)
IRM
56.4 (0.8)
74.3 (0.1)
54.2 (0.8)
71.5 (0.3)
54.7 (0.0)
72.9 (0.2)
52.4 (0.8)
70.5 (0.3)
Group DRO
57.8 (0.8)
73.7 (0.6)
54.7 (0.0)
70.7 (0.6)
55.8 (1.0)
72.5 (0.3)
53.3 (0.0)
70.0 (0.5)
Reweighted (label)
55.1 (0.8)
71.9 (0.4)
52.1 (0.2)
69.1 (0.5)
54.4 (0.4)
70.7 (0.4)
52.0 (0.0)
68.6 (0.6)
Figure 27:
Distribution of per-reviewer accuracy on the test set for the ERM model (blue). The corresponding random baseline would have per-reviewer accuracy distribution in grey.
##### Model.
For all experiments, we finetuned DistilBERT-base-uncased models (Sanh et al., [2019](#bib.bib330)), using the implementation from Wolf et al. ([2019](#bib.bib405)), and with the following hyperparameter settings:
batch size 8; learning rate 1×10−51superscript1051\times 10^{-5}1 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT with the AdamW optimizer (Loshchilov and Hutter, [2019](#bib.bib247)); L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strength 0.010.010.010.01; 3 epochs with early stopping; and a maximum number of tokens of 512.
We selected the above hyperparameters based on a grid search over learning rates {1×10−6,2×10−6,1×10−5,2×10−5}1superscript1062superscript1061superscript1052superscript105\{1\times 10^{-6},2\times 10^{-6},1\times 10^{-5},2\times 10^{-5}\}{ 1 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 2 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 1 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 2 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT }, and all other hyperparameters were simply set to standard/default values.
##### ERM results and performance drops.
A DistilBERT-base-uncased model trained with the standard ERM objective performs well on average, but performance varies widely across reviewers (Figure [27](#S5.F27 "Figure 27 ‣ E.9.2 Baseline results ‣ E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), Table [23](#S5.T23 "Table 23 ‣ E.9.2 Baseline results ‣ E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
Despite the high average accuracy of 71.9%, per-reviewer accuracies vary widely between 100.0% and 12.0%, with accuracy at the 10th percentile of 53.8%.
The above variation is larger than expected from randomness: a random binomial baseline with equal average accuracy would have a 10th percentile accuracy of 65.4%.
We observe low tail performance on both previously seen and unseen reviewers, with low 10th percentile accuracy on in-distribution and out-of-distribution sets (Table [23](#S5.T23 "Table 23 ‣ E.9.2 Baseline results ‣ E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
In addition, we observe drops on both average and 10th percentile accuracies upon evaluating on unseen reviewers, as evident in the performance gaps between the in-distribution and the out-of-distribution sets.
As with CivilComments-wilds, the relatively small number of reviews per reviewer makes it difficult to run a test-to-test comparison (e.g., training a model on just the reviewers in the bottom 10th percentile).
Without running the test-to-test comparison, it is possible that the gap between average and 10th percentile accuracies can be explained at least in part by differences in the intrinsic difficulty of reviews from different reviewers,
e.g., some reviewers might not write text reviews that are informative of their star rating.
Future work will be required to establish in-distribution accuracies that account for these differences.
##### Additional baseline methods.
We now consider models trained by existing robust training algorithms and show that these models also perform poorly on tail reviewers, failing to mitigate the performance drop (Table [23](#S5.T23 "Table 23 ‣ E.9.2 Baseline results ‣ E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
We observe that reweighting to achieve uniform class balance fails to improve the 10th percentile accuracy, showing that variation across users cannot be solved simply by accounting for label imbalance.
In addition, CORAL, IRM, and Group DRO fail to improve both average and 10th percentile accuracies on both ID and OOD sets.
Our grid search selected λ=1.0𝜆1.0\lambda=1.0italic\_λ = 1.0 for the CORAL penalty and λ=1.0𝜆1.0\lambda=1.0italic\_λ = 1.0 for the IRM penalty.
##### Discussion.
The distribution shift and the evaluation criteria for Amazon-wilds focus on the tail performance, unlike the other datasets in Wilds.
Because of this, Amazon-wilds might have distinct empirical trends or be conducive to different algorithms compared to other datasets.
Potential approaches include extensions to algorithms for worst-group performance, for example to handle a large number of groups, as well as adaptive approaches that yield user-specific predictions.
####
E.9.3 Broader context
Performance disparities across individuals have been observed in a wide range of tasks and applications, including in natural language processing (Geva et al., [2019](#bib.bib146)),
automatic speech recognition (Koenecke et al., [2020](#bib.bib208); Tatman, [2017](#bib.bib366)), federated learning (Li et al., [2019b](#bib.bib235); Caldas et al., [2018](#bib.bib72)), and medical imaging (Badgeley et al., [2019](#bib.bib24)).
These performance gaps are practical limitations in applications that call for good performance across a wide range of users,
including many user-facing applications such as speech recognition (Koenecke et al., [2020](#bib.bib208); Tatman, [2017](#bib.bib366)) and personalized recommender systems (Patro et al., [2020](#bib.bib288)),
tools used for analysis of individuals such as sentiment classification in computational social science (West et al., [2014](#bib.bib401)) and user analytics (Lau et al., [2014](#bib.bib225)),
and applications in federated learning.
These performance disparities have also been studied in the context of algorithmic fairness,
including in the federated learning literature,
in which uniform performance across individuals is cast as a goal toward fairness (Li et al., [2019b](#bib.bib235); Dwork et al., [2012](#bib.bib120)).
Lastly, these performance disparities can also highlight models’ failures to learn the actual task in a generalizable manner;
instead, some models have been shown learn the biases specific to individuals.
Prior work has shown that individuals—technicians for medical imaging in this case—can not only be identified from data, but also are predictive of the diagnosis, highlighting the risk of learning to classify technicians rather than the medical condition (Badgeley et al., [2019](#bib.bib24)).
More directly,
across a few natural language processing tasks where examples are annotated by crowdworkers, models have been observed to perform well on annotators that are commonly seen at training time, but fail to generalize to unseen annotators,
suggesting that models are merely learning annotator-specific patterns and not the task (Geva et al., [2019](#bib.bib146)).
####
E.9.4 Additional details
Table 24: Dataset details for Amazon-wilds.
| | | | |
| --- | --- | --- | --- |
| Split | # Reviews | # Reviewers | # Reviews per reviewer (mean / minimum) |
| Training | 245,502 | 1,252 | 196 / 75 |
| Validation (OOD) | 100,050 | 1,334 | 75 / 75 |
| Test (OOD) | 46,950 | 662 | 75 / 75 |
| Validation (ID) | 100,050 | 1,334 | 75 / 75 |
| Test (ID) | 46,950 | 662 | 75 / 75 |
##### Data processing.
We consider a modified version of the Amazon reviews dataset (Ni et al., [2019](#bib.bib274)).
We consider disjoint reviewers between the training, OOD validation, and OOD test sets, and we also provide separate ID validation and test sets that include reviewers seen during training for additional reporting.
These reviewers are selected uniformly at random from the reviewer pool, with the constraint that they have at least 150 reviews in the pre-processed dataset.
Statistics for each split are described in Table [24](#S5.T24 "Table 24 ‣ E.9.4 Additional details ‣ E.9 Amazon-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Notably, each reviewer has at least 75 reviews in the training set and exactly 75 reviews in the validation and test sets.
To process the data, we first eliminate reviews that are longer than 512 tokens, reviews without any text, and any duplicate reviews with identical star rating, reviewer ID, product ID, and time.
We then obtain the 30-core subset of the reviews, which contains the maximal set of reviewers and products such that each reviewer and product has at least 30 reviews; this is a standard preprocessing procedure used in the original dataset (Ni et al., [2019](#bib.bib274)).
To construct the dataset for reviewer shifts in particular, we further eliminate the following reviews:
(i) reviews that contain HTML,
(ii) reviews with identical text within a user in order to ensure sufficiently high effective sample size per reviewer,
and (iii) reviews with identical text across users to eliminate generic reviews.
Once we have the filtered set of reviews, we consider reviewers with at least 150 reviews and sample uniformly at random until the training set contains approximately 250,000 reviews and each evaluation set contains at least 100,000 reviews.
As we construct the training set, we reserve a random sample of 75 reviews for each user for evaluation and put all other reviews in the training set.
For the evaluation set, we put a random sample of 75 reviews for each user.
##### Modifications to the original dataset.
The original dataset does not prescribe a specific task or split.
We consider a standard task of sentiment classification, but instead of using a standard i.i.d. split, we instead consider disjoint users between training and evaluation time as described above.
In addition, we preprocess the data as detailed above.
###
E.10 Py150-wilds
Code completion models—autocomplete tools used by programmers to suggest subsequent source code tokens, such as the names of API calls—are commonly used to reduce the effort of software development (Robbes and Lanza, [2008](#bib.bib317); Bruch et al., [2009](#bib.bib62); Nguyen and Nguyen, [2015](#bib.bib273); Proksch et al., [2015](#bib.bib300); Franks et al., [2015](#bib.bib132)).
These models are typically trained on data collected from existing codebases but then deployed more generally across other codebases, which may have different distributions of API usages (Nita and Notkin, [2010](#bib.bib275); Proksch et al., [2016](#bib.bib301); Allamanis and Brockschmidt, [2017](#bib.bib10)). This shift across codebases can cause substantial performance drops in code completion models.
Moreover, prior studies of real-world usage of code completion models have noted that these models can generalize poorly on some important subpopulations of tokens such as method names (Hellendoorn et al., [2019](#bib.bib170)).
We study this problem using a variant of the Py150 Dataset, originally developed by Raychev et al. ([2016](#bib.bib306)) and adapted to a code completion task by Lu et al. ([2021](#bib.bib248)).
####
E.10.1 Setup
##### Problem setting.
We consider a hybrid domain generalization and subpopulation shift problem, where the domains are codebases (GitHub repositories), and our goal is to learn code completion models that generalize to source code written in new codebases.
Concretely, the input x𝑥xitalic\_x is a sequence of source code tokens taken from a single file, the label y𝑦yitalic\_y is the next token (e.g., "environ", "communicate" in Figure [12](#S4.F12 "Figure 12 ‣ 4.3.4 Py150-wilds: Code completion across different codebases ‣ 4.3 Hybrid datasets ‣ 4 Wilds datasets ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), and the domain d𝑑ditalic\_d is an integer that identifies the repository that the source code belongs to.
We aim to solve both a domain generalization problem across codebases and improve subpopulation performance on class and methods tokens.
##### Data.
The dataset comprises 150,000 Python source code files from 8,421 different repositories on GitHub ([github.com](https://github.com/)). Each source code file is associated with the repository ID so that code from the same repository can be linked.
We split the dataset by randomly partitioning the data by repositories:
1. 1.
Training: 79,866 code files from 5,477 repositories.
2. 2.
Validation (OOD): 5,160 code files from different 261 repositories.
3. 3.
Test (OOD): 39,974 code files from different 2,471 repositories.
4. 4.
Validation (ID): 5,000 code files from the same repositories as the training set (but different files).
5. 5.
Test (ID): 20,000 code files from the same repositories as the training set (but different files).
The repositories are randomly distributed across the training, validation (OOD), and test (OOD) sets.
As we use models pre-trained on the CodeSearchNet dataset (Husain et al., [2019](#bib.bib185)), which partially overlaps with the Py150 dataset, we ensured that all GitHub repositories used in CodeSearchNet only appear in the training set in Py150-wilds and not in the validation/test sets.
Table [25](#S5.T25 "Table 25 ‣ Data. ‣ E.10.1 Setup ‣ E.10 Py150-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows the token statistics of the source code files, as well as the token type breakdown (e.g., class, method, punctuator, keyword, literal).
The tokens are defined by the built-in Python tokenizer and the CodeGPT tokenizer, following Lu et al. ([2021](#bib.bib248)).
Training and evaluation are conducted at the token-level (more details are provided below).
Table 25: Token statistics for Py150-wilds.
| | | | | | | | |
| --- | --- | --- | --- | --- | --- | --- | --- |
| Split | #Files | #Total tokens | #Class | #Method | #Punctuator | #Keyword | #Literal |
| Training | 79,866 | 14,129,619 | 894,753 | 789,456 | 4,512,143 | 1,246,624 | 1,649,653 |
| Validation (ID) | 5,000 | 882,745 | 55,645 | 48,866 | 282,568 | 77,230 | 105,456 |
| Test (ID) | 20,000 | 3,539,524 | 222,822 | 194,293 | 1,130,607 | 313,008 | 420,232 |
| Validation (OOD) | 5,160 | 986,638 | 65,237 | 56,756 | 310,914 | 84,677 | 111,282 |
| Test (OOD) | 39,974 | 7,340,433 | 444,713 | 412,700 | 2,388,151 | 640,939 | 869,083 |
##### Evaluation.
We evaluate models by their accuracy on predicting class and method tokens in the test set code files. This subpopulation metric is inspired by Hellendoorn et al. ([2019](#bib.bib170)), which finds that in real-world settings, developers primarily use code completion tools for completing class names and method names;
in contrast, measuring average token accuracy would prioritize common tokens such as punctuators, which are often not a problem in real-world settings.
##### Potential leverage.
We provide the GitHub repository that each source code files was derived from, which training algorithms can leverage.
As programming tools like code completion are expected to be used across codebases in real applications (Nita and Notkin, [2010](#bib.bib275); Allamanis and Brockschmidt, [2017](#bib.bib10)), it is important for models to learn generalizable representations of code and extrapolate well on unseen codebases.
We hope that approaches using the provided repository annotations can learn to factor out common features and codebase-specific features, resulting in more robust models.
Additionally, besides the (integer) IDs of repositories, we also provide the repository names and file names in natural language as extra metadata. While we only use the repository IDs in our baseline experiments described below, the extra natural language annotations can potentially be leveraged as well to adapt models to target repositories/files.
####
E.10.2 Baseline results
##### Model.
For all experiments, we use the CodeGPT model (Lu et al., [2021](#bib.bib248)) pre-trained on CodeSearchNet (Husain et al., [2019](#bib.bib185)) as our model and finetune it on Py150-wilds, using all the tokens in the training set.
We tokenize input source code by the CodeGPT tokenizer and take blocks of length 256 tokens.
We then train the CodeGPT model with a batch size of 6 (with 6×256=1,536625615366\times 256=1,5366 × 256 = 1 , 536 tokens), a learning rate of 8×10−58superscript1058\times 10^{-5}8 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT, no L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT regularization, and the AdamW optimizer (Loshchilov and Hutter, [2019](#bib.bib247)) for 3 epochs with early stopping.
Using the hyperparameters from Lu et al. ([2021](#bib.bib248)) as a starting point, we selected the above hyperparameters by a grid search over learning rates {8×10−4,8×10−5,8×10−6}8superscript1048superscript1058superscript106\{8\times 10^{-4},8\times 10^{-5},8\times 10^{-6}\}{ 8 × 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT , 8 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 8 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT } and L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT regularization strength {0,0.01,0.1}00.010.1\{0,0.01,0.1\}{ 0 , 0.01 , 0.1 }. All other hyperparameters were simply set to standard/default values.
##### ERM results and performance drops.
Table [26](#S5.T26 "Table 26 ‣ Additional baseline methods. ‣ E.10.2 Baseline results ‣ E.10 Py150-wilds ‣ E Additional dataset details and results ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows that model performance on class and method tokens dropped substantially from 75.4% on the train-to-train in-distribution repositories in the Test (ID) set to 67.9% on the out-of-distribution repositories in the Test (OOD) set.
This gap shrinks if we evaluate the model on all tokens (instead of class and method tokens): accuracy drops from 74.5% on Test (ID) to 69.6% on Test (OOD). This is because the evaluation across all tokens includes many tokens that are used universally across repositories, such as punctuators and keywords.
We only ran a train-to-train comparison because there are a relatively large number of domains (repositories) split i.i.d. between the training and test sets, which suggests that the training and test sets should be “equally difficult”.
We therefore do not expect test-to-test and mixed-to-test comparisons to yield significantly different results.
##### Additional baseline methods.
We trained CORAL, IRM, and Group DRO baselines, treating each repository as a domain. For CORAL and IRM, we find that the smaller penalties give slightly better generalization performance (λ=1𝜆1\lambda=1italic\_λ = 1 for CORAL and λ=1𝜆1\lambda=1italic\_λ = 1 for IRM).
Compared to the ERM baseline, while CORAL and IRM reduced the performance gap between ID and OOD, neither of them improved upon ERM on the final OOD performance.
Table 26: Baseline results on Py150-wilds. We report both the model’s accuracy on predicting class and method tokens and accuracy on all tokens trained using ERM, CORAL, IRM and group DRO. Standard deviations over 3 trials are in parentheses.
| | | | | |
| --- | --- | --- | --- | --- |
| | Validation (ID) | Validation (OOD) | Test (ID) | Test (OOD) |
| Algorithm | Method/class | All | Method/class | All | Method/class | All | Method/class | All |
| ERM | 75.5 (0.5) | 74.6 (0.4) | 68.0 (0.1) | 69.4 (0.1) | 75.4 (0.4) | 74.5 (0.4) | 67.9 (0.1) | 69.6 (0.1) |
| CORAL | 70.7 (0.0) | 70.9 (0.1) | 65.7 (0.2) | 67.2 (0.1) | 70.6 (0.0) | 70.8 (0.1) | 65.9 (0.1) | 67.9 (0.0) |
| IRM | 67.3 (1.1) | 68.4 (0.7) | 63.9 (0.3) | 65.6 (0.1) | 67.3(1.1) | 68.3 (0.7) | 64.3 (0.2) | 66.4 (0.1) |
| Group DRO | 70.8 (0.0) | 71.2 (0.1) | 65.4 (0.0) | 67.3 (0.0) | 70.8 (0.0) | 71.0 (0.0) | 65.9 (0.1) | 67.9 (0.0) |
####
E.10.3 Broader context
Machine learning can aid programming and software engineering in various ways:
automatic code completion (Raychev et al., [2014](#bib.bib305); Svyatkovskiy et al., [2019](#bib.bib360)),
program synthesis (Bunel et al., [2018](#bib.bib66); Kulal et al., [2019](#bib.bib212)),
program repair (Vasic et al., [2019](#bib.bib383); Yasunaga and Liang, [2020](#bib.bib421)),
code search (Husain et al., [2019](#bib.bib185)),
and code summarization (Allamanis et al., [2015](#bib.bib11)).
However, these systems face several forms of distribution shifts when deployed in practice.
One major challenge is the shifts across codebases (which our Py150-wilds dataset focuses on), where systems need to adapt to factors such as project content, coding conventions, or library or API usage in each codebase (Nita and Notkin, [2010](#bib.bib275); Allamanis and Brockschmidt, [2017](#bib.bib10)).
A second source of shifts is programming languages, which includes adaptation across different domain-specific languages (DSLs), e.g., in robotic environments (Shin et al., [2019](#bib.bib344));
and across different versions of languages, e.g., Python 2 and 3 (Malloy and Power, [2017](#bib.bib255)).
Another challenge is the shift from synthetic training sets to real usage: for instance, Hellendoorn et al. ([2019](#bib.bib170)) show that existing code completion systems, which are typically trained as language models on source code, perform poorly on the real completion instances that are most commonly used by developers in IDEs, such as API calls (class and method calls).
####
E.10.4 Additional details
##### Data split.
We generate the splits in the following steps. First, to avoid test set contamination, we took all of the repositories in CodeSearchNet (which, as a reminder, is used to pretrain our baseline model) and assigned them to the training set. Second, we randomly split all of the remaining repositories into three groups: Validation (OOD), Test (OOD), and Others. Finally, to generate the ID splits, we randomly split the files in the Others repositories into three sets: Training, Validation (ID), and Test (ID).
##### Modifications to the original dataset.
The original Py150 dataset (Raychev et al., [2016](#bib.bib306)) splits the total 150k files into 100k training files and 50k test files,
regardless of the repository that each file was from.
In Py150-wilds, we re-split the dataset based on repositories to construct the aforementioned train, validation (ID), validation (OOD), test (ID), and test (OOD) sets.
Additionally, in the Py150 code completion task introduced in Lu et al. ([2021](#bib.bib248)), models are evaluated by the accuracy of predicting every token in source code. However, according to developer studies, this evaluation may include various tokens that are rarely used in real code completion, such as punctuators, strings, numerals, etc. (Robbes and Lanza, [2008](#bib.bib317); Proksch et al., [2016](#bib.bib301); Hellendoorn et al., [2019](#bib.bib170)).
To define a task closer to real applications, in Py150-wilds we focus on class name and method name prediction (which are used most commonly by developers).
F Datasets with distribution shifts that do not cause performance drops
------------------------------------------------------------------------
###
F.1 SQF: Criminal possession of weapons across race and locations
In this section, we provide more details on the stop-and-frisk dataset discussed in Section [8.1](#S8.SS1 "8.1 Algorithmic fairness ‣ 8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
The original data was provided by the New York City Police Department, and has been widely used in previous ML and data analysis work (Goel et al., [2016](#bib.bib150); Zafar et al., [2017](#bib.bib426); Pierson et al., [2018](#bib.bib296); Kallus and Zhou, [2018](#bib.bib197); Srivastava et al., [2020](#bib.bib351)).
For our analysis, we use the version of the dataset that was processed by Goel et al. ([2016](#bib.bib150)). Our problem setting and dataset structure closely follow theirs.
####
F.1.1 Setup
##### Problem setting.
We study a subpopulation shift in a weapons prediction task, where each data point corresponds to a pedestrian who was stopped by the police on suspicion of criminal possession of a weapon. The input x𝑥xitalic\_x is a vector that represents 29 observable features from the UF-250 stop-and-frisk form filled out by the officer after each stop: e.g., whether the stop was initiated based on a radio run or at an officer’s discretion, whether the officer was uniformed, and any reasons the officer gave for the stop (encoded as a categorical variable). Importantly, these features can all be observed by the officer prior to making the stop.999When we consider subpopulation shifts over race groups, the input x𝑥xitalic\_x additionally includes 75 one-hot indicators corresponding to the precinct that the stop was made in.
We do not include those features when we consider shifts over locations,
as they prevent the model from generalizing to new locations.
The binary label y𝑦yitalic\_y is whether the pedestrian in fact possessed a weapon (i.e., whether the stop fulfilled its stated purpose).
We consider, separately, two types of domains d𝑑ditalic\_d: 1) race groups and 2) locations (boroughs in New York City). We consider location and race as our domains because previous work has shown that they can produce substantial disparities in policing practices and in algorithmic performance (Goel et al., [2016](#bib.bib150)).
##### Data.
Each row of the dataset represents one stop of one pedestrian. Following Goel et al. ([2016](#bib.bib150)), we filter for the 621,696 stops where the reason for the stop is suspicion of criminal possession of a weapon. We then filter for rows with complete data for observable features; with stopped pedestrians who are Black, white, or Hispanic; and who are stopped during the years 2009-2012 (the time range used in Goel et al. ([2016](#bib.bib150))). These filters yield a total of 506,283 stops,
3.5% of which are positive examples (in which the officer finds that the pedestrian is illegally possessing a weapon).
The training versus validation split is a random 80%-20% partition of all stops in 2009 and 2010. We test on stops from 2011-2012; this follows the experimental setup in Goel et al. ([2016](#bib.bib150)). Overall, our data splits are as follows:
1. 1.
Training: 241,964 stops from 2009 and 2010.
2. 2.
Validation: 60,492 stops from 2009 and 2010, disjoint from the training set.
3. 3.
Test: 289,863 stops from 2011 and 2012.
In the experiments below, we do not use the entire training set,
as we observed in our initial experiments that the model performed less well on certain subgroups (Black pedestrians and pedestrians from the Bronx).
To determine whether this inferior performance might be ameliorated by training specifically on those groups, we controlled for training set size by downsampling the training set to the size of the disadvantaged population of interest for a given split.
Specifically, we consider the following (overlapping) training subsets, each of which is subsampled from the overall training set described above:
1. 1.
Black pedestrians only: 155,929 stops of Black pedestrians from 2009 and 2010.
2. 2.
All pedestrians, subsampled to # Black pedestrians: 155,929 stops of all pedestrians from 2009 and 2010.
3. 3.
Bronx pedestrians only: 69,129 stops of pedestrians in the Bronx from 2009 and 2010.
4. 4.
All pedestrians, subsampled to # Bronx pedestrians: 69,129 stops of all pedestrians from 2009 and 2010.
These amount to running a test-to-test comparison for the subpopulations of Black pedestrians and Bronx pedestrians.
##### Evaluation.
Our metric for classifier performance is the precision for each race group and each borough at a global recall
of 60%—i.e., when using a threshold which recovers 60% of all weapons in the test data, similar to the recall evaluated in Goel et al. ([2016](#bib.bib150)).
The results are similar when using different recall thresholds.
Examining the precision for each race/borough captures the fact, discussed in Goel et al. ([2016](#bib.bib150)), that very low-precision stops may violate the Fourth Amendment, which requires *reasonable suspicion* for conducting a police stop; thus, the metric encapsulates the intuition that the police are attempting to avoid Fourth Amendment violations for any race group or borough while still recovering a substantial fraction of the illegal weapons.
####
F.1.2 Baseline results
##### Model.
For all experiments, we use a logistic regression model trained with the Adam optimizer (Kingma and Ba, [2015](#bib.bib207)) and early stopping.
We trained one model on each of the 4 training sets, separately picking hyperparameters through a grid search across 7 learning rates logarithmically-spaced in [5×10−8,5×10−2]5superscript1085superscript102[5\times 10^{-8},5\times 10^{-2}][ 5 × 10 start\_POSTSUPERSCRIPT - 8 end\_POSTSUPERSCRIPT , 5 × 10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT ] and batch sizes in {4,8,16,32,64}48163264\{4,8,16,32,64\}{ 4 , 8 , 16 , 32 , 64 }.
Table [29](#S6.T29 "Table 29 ‣ ERM results and performance drops. ‣ F.1.2 Baseline results ‣ F.1 SQF: Criminal possession of weapons across race and locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") provides the hyperparameters used for each training set.
All models were trained with a reweighted cross-entropy objective that upsampled the positive examples to achieve class balance.
##### ERM results and performance drops.
Performance differed substantially across race and location groups: precision was lowest on Black pedestrians (Table [27](#S6.T27 "Table 27 ‣ ERM results and performance drops. ‣ F.1.2 Baseline results ‣ F.1 SQF: Criminal possession of weapons across race and locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), top row) and pedestrians in the Bronx (Table [28](#S6.T28 "Table 28 ‣ ERM results and performance drops. ‣ F.1.2 Baseline results ‣ F.1 SQF: Criminal possession of weapons across race and locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), top row).
To assess whether in-distribution training would improve performance on these groups, we trained the model only on Black pedestrians (Table [27](#S6.T27 "Table 27 ‣ ERM results and performance drops. ‣ F.1.2 Baseline results ‣ F.1 SQF: Criminal possession of weapons across race and locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), bottom row) and pedestrians in the Bronx (Table [28](#S6.T28 "Table 28 ‣ ERM results and performance drops. ‣ F.1.2 Baseline results ‣ F.1 SQF: Criminal possession of weapons across race and locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), bottom row).
However, this did not substantially improve performance on Black pedestrians or pedestrians from the Bronx; the difference in precision was less than 0.005 for both groups relative to the original model trained on all races and locations.
This is consistent with the fact that groups with the lowest performance are not necessarily small minorities of the dataset: for example, more than 90% of the stops are of Black or Hispanic pedestrians, but performance on these groups is worse than that for white pedestrians.
The lack of improvement from in-distribution training suggests that approaches like group DRO would be unlikely to further improve performance, and we thus did not assess these approaches.
Table 27: Comparison of precision scores for each race group at 60% global weapon recall. Train set size is 69,129 for both rows.
| | |
| --- | --- |
| | Precision at 60% recall |
| Training dataset | Black | Hispanic | White |
| Black pedestrians only | 0.131 | 0.174 | 0.360 |
| All pedestrians, subsampled to # Black pedestrians | 0.135 | 0.183 | 0.362 |
Table 28: Comparison of precision scores for each borough at a threshold which achieves 60% global weapon recall. Train set size is 155,929 for both rows.
| | |
| --- | --- |
| | Precision at 60% recall |
| Training dataset | Bronx | Brooklyn | Manhattan | Queens | Staten Island |
| Bronx pedestrians only | 0.074 | 0.158 | 0.207 | 0.157 | 0.105 |
| All pedestrians, subsampled to # Bronx pedestrians | 0.075 | 0.162 | 0.224 | 0.168 | 0.107 |
Table 29: Model parameters used in this analysis.
| | | | |
| --- | --- | --- | --- |
| Training data | Batch size | Learning rate | Number of epochs |
| Black pedestrians only | 4 | 5×10−45superscript1045\times 10^{-4}5 × 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT | 1 |
| All pedestrians, subsampled to # Black pedestrians | 4 | 5×10−45superscript1045\times 10^{-4}5 × 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT | 4 |
| Bronx pedestrians only | 4 | 5×10−45superscript1045\times 10^{-4}5 × 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT | 2 |
| All pedestrians, subsampled to # Bronx pedestrians | 4 | 5×10−35superscript1035\times 10^{-3}5 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 4 |
##### Discussion.
We observed large disparities in performance across race and location groups. However, the fact that test-to-test in-distribution training did not ameliorate these disparities suggests that they do not occur because some groups comprise small minorities of the original dataset, and thus suffer worse performance. Instead, our results suggest that classification performance on some race and location groups are intrinsically noisier; it is possible, for example, that collection of additional features would be necessary to improve performance on these groups (Chen et al., [2018](#bib.bib80)).
####
F.1.3 Additional details
##### Modifications to the original dataset.
The features we use are very similar to those used in Goel et al. ([2016](#bib.bib150)). The two primary differences are that 1) we remove features which convey information about a stopped pedestrian’s race, since those might be illegal to use in real-world policing contexts and 2) we do not include a “local hit rate” feature which captures the fraction of historical stops in the vicinity of a stop which resulted in discovery of a weapon; we omit this latter feature because it was unnecessary to match performance in Goel et al. ([2016](#bib.bib150)).
test-to-test
###
F.2 ENCODE: Transcription factor binding across different cell types
Here we provide details on the transcription factor binding dataset discussed in Section [8.3](#S8.SS3 "8.3 Genomics ‣ 8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Transcription factors (TFs) are regulatory proteins that bind specific DNA elements in the genome to activate or repress transcription of target genes.
There are estimated to be approximately 1,600 human TFs, and the binding landscape of each TF can be highly variable across different cell types (Deplancke et al., [2016](#bib.bib108)).
Understanding how these binding patterns change across different cell types and affect cellular function is critical for understanding the mechanics of dynamic gene regulation across cell types and across healthy and diseased cell states.
Several experimental strategies have been developed to profile genome-wide binding landscapes of individual TFs in specific cell types of interest.
However, genome-wide profiling of TF binding is challenging in practice, as it requires large numbers of cells and reagents (e.g., high-affinity antibodies) that are difficult and expensive to acquire.
Moreover, profiling each individual TF requires a separate experiment, so it can be prohibitively costly to map out even a few different TFs out of the >1000 in the human genome.
Therefore, there has been wide interest in computational approaches that can predict the genome-wide binding maps of multiple TFs in new cell types from a single and more practical genome-wide assay.
DNA sequence is one of the principal determinants of where a TF binds along the genome,101010Most TFs, including the ones we provide in this benchmark, have DNA-binding domains which bind to sequence motifs: short recognition sequences (4-20 bases in length) in the genome with specific binding affinity distributions (Stormo and Zhao, [2010](#bib.bib353)).
and many ML models have been developed to predict TF binding as a function of DNA sequence in a particular cell type (Alipanahi et al., [2015](#bib.bib9); Quang and Xie, [2019](#bib.bib303); Avsec et al., [2021b](#bib.bib21)).
However, even when the DNA sequence is invariant across different cell types (e.g., among cell types from the same organism), the TF binding landscape can still be highly variable (Deplancke et al., [2016](#bib.bib108)).
Therefore, TF binding models that only use sequence inputs cannot make different predictions for the same sequence across different cell types;
we also need complementary, cell-type-specific inputs to model changes in binding over different cell types.
In this section, we explore the use of genome-wide chromatin accessibility assays such as DNase-seq and ATAC-seq (Boyle et al., [2008](#bib.bib58); Thurman et al., [2012](#bib.bib373); Buenrostro et al., [2013](#bib.bib64)), in conjunction with DNA sequence, to predict TF binding.
DNA is typically accessible in a highly local and cell-type-specific manner,
and in particular, genomic sequences with high accessibility are typically bound by one or more TFs, although the identity of the TF is not directly measured by the experiment (Lee et al., [2004](#bib.bib227)).
By measuring chromatin accessibility at each base in the genome in a specific cell type of interest, we can obtain a cell-type-specific profile of binding locations; moreover, these experiments are often cheaper than profiling even a single TF (Minnoye et al., [2021](#bib.bib266)).
Our goal is to use this accessibility signal, combined with DNA sequence, to accurately predict the binding patterns of multiple TFs in new cell types.
We study the problem of predicting genome-wide TF binding across different cell types using data from the ENCODE-DREAM Transcription Factor Binding Site Prediction Challenge (Balsubramani et al., [2020](#bib.bib27)).
####
F.2.1 Setup
##### Problem setting.
We consider the domain generalization setting, where the domains are cell types, and we seek to learn models that can generalize to cell types that are not in the training set.
The task is to predict if a particular transcription factor (TF) would bind to a particular genomic location in a cell type of interest (Figure [28](#S6.F28 "Figure 28 ‣ Problem setting. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The input is DNA sequence (which we assume to be shared across all cell types) and a cell-type-specific biochemical measurement of chromatin accessibility obtained through the DNase-seq assay.
Concretely, we segment the genome into uniformly-sized, overlapping bins that are 200 base pairs (bp) in length, and tiled 50bp apart. Given a TF p𝑝pitalic\_p, each genomic bin i𝑖iitalic\_i in cell type d𝑑ditalic\_d has a binding status yi,dp∈{0,1}subscriptsuperscript𝑦𝑝𝑖𝑑01y^{p}\_{i,d}\in\{0,1\}italic\_y start\_POSTSUPERSCRIPT italic\_p end\_POSTSUPERSCRIPT start\_POSTSUBSCRIPT italic\_i , italic\_d end\_POSTSUBSCRIPT ∈ { 0 , 1 }.
Our goal is to predict each bin’s binding status as a function of the local DNA sequence Sisubscript𝑆𝑖S\_{i}italic\_S start\_POSTSUBSCRIPT italic\_i end\_POSTSUBSCRIPT and the local cell-type specific accessibility profile Ai,dsubscript𝐴𝑖𝑑A\_{i,d}italic\_A start\_POSTSUBSCRIPT italic\_i , italic\_d end\_POSTSUBSCRIPT (Figure [28](#S6.F28 "Figure 28 ‣ Problem setting. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")). We treat each TF separately, i.e., for each p𝑝pitalic\_p, we have separate training and test sets and separate models.
For computational convenience, we consider input examples x∈ℝ12800×5𝑥superscriptℝ128005x\in\mathbb{R}^{12800\times 5}italic\_x ∈ blackboard\_R start\_POSTSUPERSCRIPT 12800 × 5 end\_POSTSUPERSCRIPT that each represent a window of 12800 bp and span several genomic bins. The first four columns of x𝑥xitalic\_x is a binary matrix representing a one-hot encoding of the four bases (A,C,G,T) of the DNA sequence at that base pair. The 5th column is a real-valued vector representing chromatin accessibility.
We tile the central 6400 bp of the window with 128 overlapping bins of length 200 bp, tiled 50 bp apart.111111This ensures that each bin has at least 3200 bp of context on either side of it for prediction.
Thus, each x𝑥xitalic\_x is associated with a target output y∈{−1,0,1}128𝑦superscript101128y\in\{-1,0,1\}^{128}italic\_y ∈ { - 1 , 0 , 1 } start\_POSTSUPERSCRIPT 128 end\_POSTSUPERSCRIPT indicating the binding status of the TF at each of these 128 bins. The three possible values at each bin indicate whether the bin is bound, unbound, or ambiguous.
During training and testing, we simply ignore ambiguous bins, and only focus on bound or unbound bins.
The domain d𝑑ditalic\_d is an integer that identifies the cell type.
Figure 28:
Setup of the ENCODE benchmark. (a) The predictive model predicts binding of a protein to a location, in a cell type (domain). (b) The input features are DNA sequence and chromatin accessibility, and the labels are assigned over 200 base pair (bp) bins tiling the genome every 50 bp. (c) Each training example is a 12800 bp window, with the 128 middle bins evaluated (spanning 6400 bp).
##### Data.
The dataset comprises (a) genome-wide sequence; (b) TF binding maps for two TFs, JUND and MAX, across a total of 6 and 8 cell types respectively; and (c) an accessibility profile for each cell type.
As described above and illustrated in Figure [28](#S6.F28 "Figure 28 ‣ Problem setting. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we break up these genome-wide data into overlapping 12800 bp windows, which each correspond to a single training example.
The central 6400 bp of each 12800 bp window is tiled with overlapping 200 bp bins that each correspond to one coordinate of the corresponding y∈{0,1}128𝑦superscript01128y\in\{0,1\}^{128}italic\_y ∈ { 0 , 1 } start\_POSTSUPERSCRIPT 128 end\_POSTSUPERSCRIPT.
These 12800 bp windows are tiled 6400 bp apart, such that each genomic location falls within the central 6400 bp region of exactly one window.
We split the examples by domain (cell type) as well as by chromosome (a large contiguous subsequence of the genome) within a cell type.
In each split, we use one cell type for the test data, one for the validation data, and the remaining cell types for the training data.
These domain-wise splits are listed in Table [30](#S6.T30 "Table 30 ‣ Data. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), and are divided into two types:
1. 1.
The *ENCODE-DREAM* splits follow the original challenge setup (Balsubramani et al., [2020](#bib.bib27)) closely in evaluating only on the cell type liver, which is a primary tissue, in contrast to all of the other cell types, which are immortalized cell lines that have been grown outside the body for many generations. This is a more realistic setting in the sense that it is easier to collect data from immortalized cell lines, which we can then use to train a model that predicts TF binding in harder-to-profile primary tissues.
However, the fact that none of the training cell types are primary tissues might limit generalization to primary tissues. Moreover, because cell types are highly variable, conclusions drawn from a single liver cell type might not generalize to other cell types.
2. 2.
We thus also use a *round-robin* set of splits, where we assign each cell type to test and validation sets in a rotating manner. This round-robin evaluation comprises several splits for each TF.
For each split in Table [30](#S6.T30 "Table 30 ‣ Data. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), the data are divided into training, validation, and test sets by chromosome:
1. 1.
Training:
323,894 windows per training cell type, before filtering. To improve class balance, we filter out windows with all 128 bins labeled negative, which typically removes over 3/4 of these training windows; the exact number filtered out depends on the split.
The training windows are taken from all chromosomes except {1,2,8,9,11,21}12891121\{1,2,8,9,11,21\}{ 1 , 2 , 8 , 9 , 11 , 21 }.
2. 2.
Validation (OOD):
27,051 windows from 1 validation cell type and from chromosomes {2,9,11}2911\{2,9,11\}{ 2 , 9 , 11 }.
3. 3.
Test (OOD):
23,109 windows from 1 test cell type and from chromosomes {1,8,21}1821\{1,8,21\}{ 1 , 8 , 21 }.
4. 4.
Validation (ID):
27,051 windows in total across all training cell types, from chromosomes {2,9,11}2911\{2,9,11\}{ 2 , 9 , 11 }.
5. 5.
Test (ID):
23,109 windows in total across all training cell types, from chromosomes {1,8,21}1821\{1,8,21\}{ 1 , 8 , 21 }.
For computational speed, the Validation (OOD) and Test (OOD) sets above were subsampled by a factor of 3 from the available raw data, while the Validation (ID) and Test (ID) sets were subsampled by a factor of 3 ×\times× the number of training cell types.
Table 30:
List of splits for which we trained models for ENCODE.
Performance of models on round-robin splits are averaged to get the summarized results in Table [32](#S6.T32 "Table 32 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
| | | | |
| --- | --- | --- | --- |
| Split name | TF name | Test cell type | Validation cell type |
| ENCODE-DREAM | MAX | liver | HepG2 |
| round-robin | MAX | K562 | liver |
| round-robin | MAX | liver | A549 |
| round-robin | MAX | A549 | GM12878 |
| round-robin | MAX | GM12878 | H1-hESC |
| round-robin | MAX | H1-hESC | HCT116 |
| round-robin | MAX | HCT116 | HeLa-S3 |
| round-robin | MAX | HeLa-S3 | HepG2 |
| round-robin | MAX | HepG2 | K562 |
| ENCODE-DREAM | JUND | liver | HepG2 |
| round-robin | JUND | K562 | liver |
| round-robin | JUND | liver | MCF-7 |
| round-robin | JUND | MCF-7 | HCT116 |
| round-robin | JUND | HCT116 | HeLa-S3 |
| round-robin | JUND | HeLa-S3 | HepG2 |
| round-robin | JUND | HepG2 | K562 |
##### Evaluation.
We evaluate models by their average precision (AP) in predicting binary binding status (excluding all ambiguous bins). Specifically, we treat each bin as a separate binary classification problem; in other words, we split up each prediction of the 128-dimensional vector y𝑦yitalic\_y into at most 128 separate binary predictions after excluding ambiguous bins. We then compute the average precision of the model on this binary classification problem.
The choice of average precision as an evaluation metric is motivated by the class imbalance (low proportion of bound/positive labels) of this binary classification problem over bins.
All splits have more than one hundred times as many unbound bins than bound bins (Table [31](#S6.T31 "Table 31 ‣ Evaluation. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
Table 31: Binding site imbalance and uniqueness (across cell types) in binary genome-wide binding datasets in ENCODE.
Third column indicates the fraction of (non-ambiguous) bins that are labeled positive.
Fourth column indicates the fraction of positive bins (bound sites) that are cell-type-specific: they are bound (or ambiguous) in at most one other cell type.
Bins are 200bp wide.
| | | | |
| --- | --- | --- | --- |
| TF name | Cell type | Frac. positive bins | Frac. cell-type-specific binding sites |
| MAX | liver | 4.90×10−34.90superscript1034.90\times 10^{-3}4.90 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.518 |
| MAX | HepG2 | 6.20×10−36.20superscript1036.20\times 10^{-3}6.20 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.331 |
| MAX | K562 | 6.46×10−36.46superscript1036.46\times 10^{-3}6.46 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.368 |
| MAX | A549 | 5.90×10−35.90superscript1035.90\times 10^{-3}5.90 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.218 |
| MAX | GM12878 | 1.93×10−31.93superscript1031.93\times 10^{-3}1.93 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.217 |
| MAX | H1-hESC | 4.44×10−34.44superscript1034.44\times 10^{-3}4.44 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.363 |
| MAX | HCT116 | 6.46×10−36.46superscript1036.46\times 10^{-3}6.46 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.237 |
| MAX | HeLa-S3 | 4.21×10−34.21superscript1034.21\times 10^{-3}4.21 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.218 |
| JUND | liver | 4.45×10−34.45superscript1034.45\times 10^{-3}4.45 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.523 |
| JUND | K562 | 3.94×10−33.94superscript1033.94\times 10^{-3}3.94 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.408 |
| JUND | HCT116 | 4.08×10−34.08superscript1034.08\times 10^{-3}4.08 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.297 |
| JUND | HeLa-S3 | 3.60×10−33.60superscript1033.60\times 10^{-3}3.60 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.323 |
| JUND | HepG2 | 3.54×10−33.54superscript1033.54\times 10^{-3}3.54 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.513 |
| JUND | MCF-7 | 1.84×10−31.84superscript1031.84\times 10^{-3}1.84 × 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT | 0.335 |
####
F.2.2 Baseline results
##### Model.
Our model is a version of the fully convolutional U-Net model for image segmentation (Ronneberger et al., [2015](#bib.bib320)), modified from the architecture in Li and Guan ([2019](#bib.bib231)). It is illustrated in Figure [29](#S6.F29 "Figure 29 ‣ Model. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
We train each model using the average cross-entropy loss over the 128 output bins in each example (after excluding ambiguous bins).
Figure 29:
Architecture of the baseline prediction model, based on U-Net.
The final layers were modified to collapse the representation down to a single channel and finally convolved with kernel size 200 and stride 50, mimicking the resolution of labels along the genome.
For hyperparameters, we searched over the learning rates {10−5,10−4,10−3}superscript105superscript104superscript103\{10^{-5},10^{-4},10^{-3}\}{ 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT }, and L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strengths {10−4,10−3,10−2}superscript104superscript103superscript102\{10^{-4},10^{-3},10^{-2}\}{ 10 start\_POSTSUPERSCRIPT - 4 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 3 end\_POSTSUPERSCRIPT , 10 start\_POSTSUPERSCRIPT - 2 end\_POSTSUPERSCRIPT }.
We use 10 replicates (with different random seeds) for all reported results.
##### ERM results.
Table [32](#S6.T32 "Table 32 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") and Table [34](#S6.T34 "Table 34 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") show the results of ERM models trained on each split.
On many individual splits (Table [34](#S6.T34 "Table 34 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), the OOD validation and OOD test performance are very different, reflecting the variability across the cell types.
On average across the round robin splits, the OOD validation performance is slightly higher than the OOD test performance, as we selected hyperparameters and did early stopping to maximize the former (Table [32](#S6.T32 "Table 32 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
We also observed high variance in training and test performance across random seeds in a few splits (e.g., the K562 / liver split for the transcription factor JUND), which suggests some optimization instability in our training protocol.
We also computed the in-distribution baselines in a train-to-train setting, i.e., on the Validation (ID) and Test (ID) splits described above.
We also ran corresponding in-distribution baselines in a test-to-test setting, i.e., we trained ERM models on data from the training chromosomes in the test cell type, and tested it on the same test set comprising data from the test chromosomes in the test cell type.121212
Prior work has shown that there is minimal variation in performance between chromosomes on this problem (Won et al., [2010](#bib.bib406); Alipanahi et al., [2015](#bib.bib9); Keilwagen et al., [2019](#bib.bib202)), so we can approximate these training and test distributions as identical.
Table [33](#S6.T33 "Table 33 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") shows these in-distribution results.
For the round-robin splits, the difference between the train-to-train and test-to-test settings is that the former trains and tests on mixtures of multiple cell types, whereas the latter trains and tests on individual cell types.
We considered two TFs, MAX and JUND, separately.
For the ENCODE-DREAM splits, both TFs showed large ID-OOD performance gaps.
However, we opted not to use the ENCODE-DREAM split as a Wilds dataset
because the variability between cell types made us cautious about over-interpreting the results on a single cell type. For example, for MAX, we found that the Validation (OOD) and Test (OOD) cell types were so different that their results were anti-correlated across different random seeds, which would have made benchmarking challenging.
Moreover, the fact that the test cell type (liver) in the ENCODE-DREAM splits was the only primary tissue might have meant that the training data might have insufficient leverage for a model to learn to close the ID-OOD gap.
We therefore focused on analyzing the round-robin splits.
For MAX, using the train-to-train comparison, the average Test (ID) and Test (OOD) AP across the round-robin splits were not significantly different (64.9 (2.1) vs. 59.6 (2.0), respectively; Table [32](#S6.T32 "Table 32 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
For JUND, using the train-to-train comparison, the average Test (ID) and Test (OOD) AP across the round-robin splits showed a larger gap (54.1 (4.2) vs. 42.9 (3.2), respectively; Table [32](#S6.T32 "Table 32 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")), but the variability in training performance made these results less reliable. Moreover, the test-to-test ID results were significantly higher than the train-to-train ID results (62.4 (2.6) vs. 54.1 (4.2), respectively), which suggests that either the model capacity or feature set is not rich enough to fit the variation across different cell types.
We therefore opted not to include the round-robin splits in Wilds as well.
Table 32: ERM baseline results on ENCODE.
All numbers are average precision.
“Round-robin” indicates the average performance over all splits marked “round-robin” in Table [30](#S6.T30 "Table 30 ‣ Data. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Parentheses show standard deviation across replicates, for liver; and average of such standard deviations across splits, for round-robin.
Expanded results per round-robin split are in Table [35](#S6.T35 "Table 35 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
| | | | | | |
| --- | --- | --- | --- | --- | --- |
| TF | Split scheme | Validation (ID) | Test (ID) | Validation (OOD) | Test (OOD) |
| MAX | ENCODE-DREAM | 70.3 (2.1) | 68.3 (1.9) | 67.9 (1.6) | 45.0 (1.5) |
| MAX | round-robin | 65.0 (2.1) | 64.9 (2.1) | 62.1 (1.2) | 59.6 (2.0) |
| JUND | ENCODE-DREAM | 65.9 (1.2) | 66.7 (1.4) | 32.9 (1.0) | 42.3 (2.5) |
| JUND | round-robin | 53.2 (4.0) | 54.1 (4.2) | 47.2 (2.4) | 42.9 (3.2) |
Table 33: In-distribution results on ENCODE: when training and validation cell types are set to the test cell type.
All numbers are average precision.
“Round-robin” indicates the average performance over all splits marked “round-robin” in Table [30](#S6.T30 "Table 30 ‣ Data. ‣ F.2.1 Setup ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
Parentheses show standard deviation across replicates, for liver; and average of such standard deviations across splits, for round-robin.
Expanded results per round-robin split are in Table [35](#S6.T35 "Table 35 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts").
| | | | | |
| --- | --- | --- | --- | --- |
| TF | Split scheme | Train | Validation (ID) | Test (ID) |
| MAX | ENCODE-DREAM | 76.1 (0.9) | 57.3 (1.2) | 57.6 (1.3) |
| MAX | round-robin | 77.3 (0.9) | 65.2 (1.3) | 65.4 (1.3) |
| JUND | ENCODE-DREAM | 76.0 (0.6) | 55.8 (0.5) | 56.0 (0.7) |
| JUND | round-robin | 79.3 (2.7) | 61.8 (2.4) | 62.4 (2.6) |
Table 34: Baseline results on ENCODE.
In-distribution (ID) results correspond to the train-to-train setting.
Parentheses show standard deviation across replicates.
| | | | | | | |
| --- | --- | --- | --- | --- | --- | --- |
| TF name | Test / Val cell type | Train AP | Val (ID) AP | Test (ID) AP | Val (OOD) AP | Test (OOD) AP |
| MAX | liver / HepG2 | 79.5 (1.0) | 70.3 (2.1) | 68.3 (1.9) | 67.9 (1.6) | 45.0 (1.5) |
| MAX | K562 / liver | 75.1 (2.3) | 59.9 (4.5) | 59.2 (3.9) | 47.6 (1.0) | 63.6 (4.5) |
| MAX | liver / A549 | 78.5 (1.3) | 68.6 (0.8) | 68.4 (0.5) | 66.6 (1.3) | 38.5 (1.1) |
| MAX | A549 / GM12878 | 78.0 (1.7) | 66.0 (2.6) | 66.6 (2.8) | 46.9 (1.9) | 65.0 (2.5) |
| MAX | GM12878 / H1-hESC | 80.0 (1.2) | 69.6 (0.8) | 69.2 (0.6) | 65.4 (0.7) | 46.3 (0.5) |
| MAX | H1-hESC / HCT116 | 75.5 (3.3) | 63.2 (3.2) | 63.9 (3.3) | 70.6 (0.5) | 61.7 (2.5) |
| MAX | HCT116 / HeLa-S3 | 76.8 (1.1) | 64.5 (1.6) | 64.9 (1.3) | 63.9 (0.9) | 69.4 (0.9) |
| MAX | HeLa-S3 / HepG2 | 77.7 (1.7) | 65.0 (1.9) | 64.8 (3.3) | 67.7 (1.9) | 64.0 (2.5) |
| MAX | HepG2 / K562 | 77.3 (1.3) | 63.2 (1.3) | 62.1 (1.4) | 68.5 (1.1) | 68.4 (1.1) |
| JUND | liver / HepG2 | 82.6 (1.3) | 65.9 (1.2) | 66.7 (1.4) | 32.9 (1.0) | 42.3 (2.5) |
| JUND | K562 / liver | 54.2 (10.5) | 29.9 (8.4) | 33.3 (8.4) | 32.9 (3.7) | 51.2 (4.5) |
| JUND | liver / MCF-7 | 83.6 (2.4) | 65.5 (3.4) | 65.3 (4.0) | 28.9 (2.7) | 29.2 (3.2) |
| JUND | MCF-7 / HCT116 | 76.4 (3.5) | 52.5 (3.4) | 53.6 (3.8) | 51.8 (3.7) | 27.2 (4.2) |
| JUND | HCT116 / HeLa-S3 | 75.7 (1.5) | 50.0 (2.4) | 50.6 (2.4) | 69.2 (2.1) | 52.9 (3.2) |
| JUND | HeLa-S3 / HepG2 | 78.0 (2.1) | 59.5 (5.1) | 60.0 (4.9) | 30.3 (1.3) | 66.6 (3.6) |
| JUND | HepG2 / K562 | 79.6 (0.9) | 61.9 (1.1) | 62.3 (1.4) | 69.8 (0.6) | 30.5 (0.6) |
Table 35: Test-to-test results on ENCODE.
Parentheses show standard deviation across replicates.
| | | | | |
| --- | --- | --- | --- | --- |
| TF name | Test cell type | Train | Val (ID) AP | Test (ID) AP |
| MAX | liver | 76.1 (0.9) | 57.3 (1.2) | 57.6 (1.3) |
| MAX | HepG2 | 76.1 (0.8) | 66.5 (1.1) | 68.4 (1.3) |
| MAX | K562 | 83.6 (0.7) | 74.7 (0.8) | 75.9 (0.7) |
| MAX | A549 | 77.2 (0.8) | 68.4 (1.4) | 67.5 (1.5) |
| MAX | GM12878 | 64.7 (0.8) | 50.9 (1.3) | 49.2 (1.5) |
| MAX | H1-hESC | 76.2 (1.8) | 65.3 (2.1) | 64.1 (1.9) |
| MAX | HCT116 | 82.8 (0.7) | 73.6 (0.8) | 74.5 (0.8) |
| MAX | HeLa-S3 | 80.5 (0.8) | 64.8 (1.4) | 66.4 (1.4) |
| JUND | liver | 76.0 (0.6) | 55.8 (0.5) | 56.0 (0.7) |
| JUND | K562 | 87.3 (1.3) | 74.5 (1.1) | 76.0 (1.7) |
| JUND | HCT116 | 80.9 (2.8) | 69.5 (4.9) | 68.4 (4.7) |
| JUND | HeLa-S3 | 87.2 (0.8) | 69.0 (0.7) | 70.9 (0.8) |
| JUND | HepG2 | 84.1 (9.8) | 71.9 (4.6) | 72.1 (4.9) |
| JUND | MCF-7 | 60.1 (0.8) | 30.1 (2.4) | 31.1 (2.9) |
##### Discussion.
Even in the in-distribution (test-to-test) setting, the results in Table [35](#S6.T35 "Table 35 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") show how
different model performance can be for different domains.
For example, the liver domain of primary tissue (from a human donor) is derived from lower-quality data than many of the long-standard cell lines (grown outside the human body) constituting other domains, and is consequently noisier than many of them (Balsubramani et al., [2017](#bib.bib26)).
The extent of this variation underscores the importance of accounting for the variability between domains when measuring the effect of distribution shift;
for example, a train-to-train comparison could lead to significantly different conclusions than a test-to-test comparison.
The effect of the distribution shift also seems to depend on the particular TF (MAX vs. JUND) used.
Biologically, different TFs show different levels of cell-type-specificity, and better understanding which TFs have binding patterns that can be accurately predicted from the cell-type-specific accessibility assays is important future work.
One of the main obstacles preventing us from using this ENCODE dataset as a Wilds benchmark is the instability in optimization that we reported above.
We speculate that this instability could, in part, be due to the class imbalance in the data, but more work will be needed to ascertain this and to develop methods for training models more reliably on this type of genomic data.
As we mentioned above, Table [32](#S6.T32 "Table 32 ‣ ERM results. ‣ F.2.2 Baseline results ‣ F.2 ENCODE: Transcription factor binding across different cell types ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") reports significantly higher test-to-test ID results than train-to-train ID results for the JUND round-robin split scheme. The main difference between the test-to-test and train-to-train settings in the round-robin splits is that the former trains and tests on a single cell type, whereas the latter trains and tests on a mixture of cell types. The fact that ID performance is significantly higher in the former than the latter suggests that the learned models are not able to fit JUND binding patterns across multiple cell types.
This could be due to a model family that is not large or expressive enough, or it could be because the feature set does not have all of the necessary information to accurately predict binding across cell types.
In either case, it is unlikely that a training algorithm developed to be robust to distribution shifts will be able to significantly improve OOD performance in this setting, as the issue seems to lie in the model family or the data distribution instead.
Overall, it is commonly understood that distribution shifts between cell types are a significant problem for TF binding prediction, and many methods have been developed to tackle these shifts (Balsubramani et al., [2017](#bib.bib26); Li et al., [2019a](#bib.bib232); Li and Guan, [2019](#bib.bib231); Keilwagen et al., [2019](#bib.bib202); Quang and Xie, [2019](#bib.bib303)).
Nonetheless, we found it challenging to establish a rigorous distribution shift benchmark around this task,
as our results were confounded by factors such as optimization issues, large variability between cell types,
and the difficulty of learning a model that could fit multiple cell types even in an i.i.d. setting.
We hope that future work on evaluating and mitigating distribution shifts in TF binding prediction
can build upon our results and address these challenges.
####
F.2.3 Additional details
##### Additional dataset details.
The ground-truth labels were derived from high-quality chromatin immunoprecipitation sequencing (ChIP-seq) experiments, which provide a genome-wide track of binding enrichment scores for each TF.
Statistical methods based on standardized pipelines (Landt et al., [2012](#bib.bib221)) were used to identify high-confidence binding events across the genome, resulting in a genome-wide track indicating whether each of the windows of sequence in the genome is bound or unbound by the TF, or whether binding is ambiguous but likely (these were ignored in our benchmarking).
Our data include two TFs chosen for their basic importance in cell-type-specific gene regulation: MAX and JUND.
MAX canonically recognizes a short, common sequence (the domain CACGTG), but its structure leads it to bind to DNA as a dimer, and facilitates cooperative activity with a range of partners (Grandori et al., [2000](#bib.bib155)) with many weaker and longer-range sequence determinants of binding (Allevato et al., [2017](#bib.bib12)).
JUND belongs to a large family of TFs (bZIP) known for binding in cooperation with partners in the family in a variety of modes, all involving a short 7bp sequence (TGA[C/G]TCA) and its two halves.
##### Additional model details.
The network consists of encoder and decoder portions:
* •
Encoder. The encoder is composed of five downscaling convolutional blocks, each consisting of two stride-1 convolutional layers with kernel size 7 (and padding such that the output size is left unchanged), followed by a max-pooling layer with kernel size 2.
Each successive block halves the input window size and scales up the number of convolutional filters (by 1.5).
* •
Decoder. Mirroring the encoder, the decoder is composed of five upscaling convolutional blocks, each consisting of two convolutional layers with kernel size 7 and an upsampling layer (a ConvTranspose layer with kernel size 2 and stride 2).
Each successive block doubles the input window size.
The respective sizes of the decoder layer representations are the same as the encoder in reverse, culminating in a (12800×15)1280015(12800\times 15)( 12800 × 15 ) representation that is then run through a convolutional layer (kernel size 200, stride 50) to reduce it to a single channel (with length 253).
A final fully-connected layer results in a 128-dimensional output.
Batch normalization is applied after every layer except the last, and each intermediate convolutional layer is padded such that the output and input sizes are equal.
##### Additional data sources.
The ENCODE-DREAM prediction challenge contains binding data for many TFs from a large range of cell types,
discretized into the same 200-bp windows used in this benchmark.
The ENCODE portal (encodeproject.org) contains more ChIP-seq datasets from the 13 challenge cell lines for which we provide DNase accessibility data.
DNA shape and gene expression data types were also provided in the original challenge.
* •
DNA shape. Twisting, bending, and shearing of DNA influence local binding in a TF-specific fashion (Rohs et al., [2009](#bib.bib318)).
* •
Gene expression. Expression levels of all human genes were provided using RNA-seq data from ENCODE. This can be used to model the presence of cofactor proteins that can recruit TFs for binding (Ptashne and Gann, [1997](#bib.bib302)).
However, none of the top challenge participants found these data modalities useful (Balsubramani et al., [2017](#bib.bib26)), so they are not provided in this benchmark.
##### Data normalization.
We normalize the distribution of each DNase-seq signal readout to the average of the DNase-seq signals over training cell types.
We use a version of quantile normalization (Bolstad et al., [2003](#bib.bib53)) with piecewise polynomial interpolation.
Li and Guan ([2019](#bib.bib231)) also use this, but instead normalize to the test domain’s DNase distribution.
As this technique uses test-domain data, it is out of the scope of our benchmark.
However, we note that in genomics settings it is realistic to have relatively cheaply available chromatin accessibility data in the target cell type of interest.
##### Modifications to the original setup.
The prediction task of the challenge was a binary classification problem over the 200 bp bins, which did not involve the fixed 12800 bp windows.
To predict on a bin, participating teams were free to use as much of the regions surrounding (flanking) the bin as they wished.
The winning teams all used at least 1000 bp total for each bin, and further work has shown the efficacy of using much larger flanking regions of tens of thousands of bp (Quang and Xie, [2019](#bib.bib303); Avsec et al., [2021a](#bib.bib20)).
We instead predict on 128 bins at once (following Li and Guan ([2019](#bib.bib231))),
which allows for more efficient training and prediction.
Our ERM baselines’ OOD test performance is competitive with the original challenge results, but lower than the state-of-the-art performance of Li and Guan ([2019](#bib.bib231)) because of the aforementioned differences in data processing, splits, and architecture, as well as the cross-domain training method employed by that paper and predecessor work (Li et al., [2019a](#bib.bib232)).
These and other state-of-the-art models noted that their domain adaptation strategies played a major role in improving performance.
###
F.3 BDD100K: Object recognition in autonomous driving across locations
As discussed in Section [8.6](#S8.SS6 "8.6 Robotics ‣ 8 Distribution shifts in other application areas ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), autonomous driving, and robotics in general, is an important
application that requires effective and robust tools for handling distribution shift. Here, we
discuss our findings on a modified version of the BDD100K dataset that evaluates on shifts based on
time of day and location. Our results below suggest that more challenging tasks, such as object
detection and segmentation, may be more suited to evaluations of distribution shifts in an
autonomous driving context.
Figure 30: For BDD100K, we study two different types of shift, based on time of day and location. We
visualize randomly chosen images and their corresponding labels from the training, validation, and
test splits for both shifts. The labels are 9-dimensional binary vectors indicating the presence
(1) or absence (0) of, in order: bicycles, buses, cars, motorcycles, pedestrians, riders, traffic
lights, traffic signs, and trucks.
Table 36: Average multi-task classification accuracy of ERM trained models on BDD100K. All
results are reported across 3 random seeds, with standard deviation in parentheses. We observe no
substantial drops in the presence of test time distribution shifts.
| | | |
| --- | --- | --- |
| | Time of day shift | Location shift |
| Algorithm | Validation (ID) | Test (OOD) | Validation (ID) | Test (OOD) |
| ERM | 87.1 (0.3) | 89.7 (0.2) | 87.9 (0.0) | 86.9 (0.0) |
####
F.3.1 Setup
##### Task.
In line with the other datasets in Wilds, we evaluate using a classification task. Specifically,
the task is to predict whether or not 9 different categories appear in the image x𝑥xitalic\_x: bicycles,
buses, cars, motorcycles, pedestrians, riders, traffic lights, traffic signs, and trucks. This is a
multi-task binary classification problem, and the label y𝑦yitalic\_y is thus a 9-dimensional binary vector.
##### Data.
The BDD100K dataset is a large and diverse driving dataset crowd-sourced from tens of thousands of
drivers, covering four different geographic regions and many different times of day, weather
conditions, and scenes (Yu et al., [2020](#bib.bib424)). The original dataset contains 80,000 images in the combined
training and validation sets and is richly annotated for a number of different tasks such as
detection, segmentation, and imitation learning. We use bounding box labels to construct our task
labels, and as discussed later, we use location and image tags to construct the shifts we evaluate.
##### Evaluation.
In evaluating the trained models, we consider average accuracy across the binary classification
tasks, averaged over each of the validation and test sets separately. We next discuss how we create
and evaluate two different types of shift based on time of day and location differences.
####
F.3.2 Time of day shift
##### Distribution shift and evaluation.
We evaluate two different types of shift, depicted in Figure [30](#S6.F30 "Figure 30 ‣ F.3 BDD100K: Object recognition in autonomous driving across locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"). For time of day
shift (Figure [30](#S6.F30 "Figure 30 ‣ F.3 BDD100K: Object recognition in autonomous driving across locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") top row), we use the original BDD100K training set, which has roughly
equal proportions of daytime and non daytime images (Yu et al., [2020](#bib.bib424)). However, we construct a test
set using the original BDD100K validation set that only includes non-daytime images. We then split
roughly the same number of images randomly from the training set to form an in-distribution
validation set,
which allows us to do a train-to-train comparison. There are 64,993, 4,860, and 4,742 images in the training, validation, and test
splits, respectively.
##### ERM results.
Table [36](#S6.T36 "Table 36 ‣ F.3 BDD100K: Object recognition in autonomous driving across locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") summarizes our findings. For time of day shift, we actually observe
slightly *higher* test performance, on only non daytime images, than validation performance on
mixed daytime and non daytime images. We contrast this with findings from
Dai and Van Gool ([2018](#bib.bib101)); Yu et al. ([2020](#bib.bib424)), who showed worse test performance for segmentation and detection tasks,
respectively, on non daytime images. We believe this disparity can be attributed to the difference
in tasks—for example, it is likely more difficult to draw an accurate bounding box for a car at
night than to simply recognize tail lights and detect the presence of a car.
####
F.3.3 Location shift
##### Distribution shift.
For location shift (Figure [30](#S6.F30 "Figure 30 ‣ F.3 BDD100K: Object recognition in autonomous driving across locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") bottom row), we combine all of the data from the
original BDD100K training and validation sets. We construct training and validation sets from all of
the images captured in New York, and we use all images from California for the test set. The
validation set again is in-distribution with respect to the training set and has roughly the same
number of images as the test set. There are 53,277, 9,834, and 9,477 images in the training,
validation, and test splits, respectively.
##### ERM results.
In the case of location shift, we see from Table [36](#S6.T36 "Table 36 ‣ F.3 BDD100K: Object recognition in autonomous driving across locations ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts") that there is a small drop in
performance, possibly because this shift is more drastic as the locations are disjoint between
training and test time. However, the performance drop is relatively small and the test time
accuracy is still comparable to validation accuracy. In general, we believe that these results lend
support to the conclusion that, for autonomous driving and robotics applications, other more
challenging tasks are better suited for evaluating performance. Generally speaking, incorporating a
wide array of different applications will likely require a simultaneous effort to incorporate
different tasks as well.
###
F.4 Amazon: Sentiment classification across different categories and time
Our benchmark dataset Amazon-wilds studies user shifts.
In Section [7](#S7 "7 Empirical trends ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), we discussed empirical trends on other types of distribution shifts on the same underlying 2018 Amazon Reviews dataset (Ni et al., [2019](#bib.bib274)).
We now present the detailed setup and empirical results for the time and category shifts.
####
F.4.1 Setup
##### Model.
For all experiments in this section, we finetune BERT-base-uncased models, using the implementation from Wolf et al. ([2019](#bib.bib405)), and with the following hyperparameter settings:
batch size 8; learning rate 2×10−62superscript1062\times 10^{-6}2 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT; L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strength 0.010.010.010.01; 3 epochs; and a maximum number of tokens of 512.
These hyperparameters are taken from the Amazon-wilds experiments.
####
F.4.2 Time shifts
##### Problem setting.
We consider the domain generalization setting, where the domain d𝑑ditalic\_d is the year in which the reviews are written.
As in Amazon-wilds, the task is multi-class sentiment classification, where
the input x𝑥xitalic\_x is the text of a review, the label y𝑦yitalic\_y is a corresponding star rating from 1 to 5.
##### Data.
The dataset is a modified version of the Amazon Reviews dataset (Ni et al., [2019](#bib.bib274)) and comprises customer reviews on Amazon.
Specifically, we consider the following split:
1. 1.
Training: 1,000,000 reviews written in years 2000 to 2013.
2. 2.
Validation (OOD): 20,000 reviews written in years 2014 to 2018.
3. 3.
Test (OOD): 20,000 reviews written in years 2014 to 2018.
To construct the above split, we first randomly sample 4,000 reviews per year for the evaluation splits. For years in which there are not sufficient reviews, we split the reviews equally between validation and test. After constructing the evaluation set, we then randomly sample from the remaining reviews to form the training set.
##### Evaluation.
To assess whether models generalize to future years, we evaluate models by their average accuracy on the OOD test set.
##### ERM results and performance drops.
We only observed modest performance drops due to time shift.
Our baseline model performs well on the OOD test set, achieving 76.0% accuracy on average and 75.4% on the worst year (Table [37](#S6.T37 "Table 37 ‣ ERM results and performance drops. ‣ F.4.2 Time shifts ‣ F.4 Amazon: Sentiment classification across different categories and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
To measure performance drops due to distribution shifts, we ran a test-to-test comparison by training a model on reviews written in years 2014 to 2018 (Table [38](#S6.T38 "Table 38 ‣ ERM results and performance drops. ‣ F.4.2 Time shifts ‣ F.4 Amazon: Sentiment classification across different categories and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The performance gaps between the model trained on the official split and the model trained on the test-to-test split are consistent but modest across the years, with the biggest drop of 1.1% for 2018.
Table 37: Baseline results on time shifts on the Amazon Reviews Dataset. We report the accuracy of models trained using ERM. In addition to the average accuracy across all years in each split, we report the accuracy for the worst-case year.
| | | | |
| --- | --- | --- | --- |
| | Train | Validation (OOD) | Test (OOD) |
| Algorithm | Average | Worst year | Average | Worst year | Average | Worst year |
| ERM | 75.0 (0.0) | 72.4 (0.1) | 75.7 (0.1) | 74.6 (0.1) | 76.0 (0.1) | 75.4 (0.1) |
Table 38: Test-to-test in-distribution comparison for time shifts on Amazon Reviews Dataset. We observe only modest performance drops due to time shifts.
| | | | | | | |
| --- | --- | --- | --- | --- | --- | --- |
| Setting | Year | 2014 | 2015 | 2016 | 2017 | 2018 |
| Official | 75.4 (0.1) | 75.8 (0.1) | 76.3 (0.1) | 76.4 (0.4) | 76.1 (0.1) | |
| Test-to-test | 76.1 (0.2) | 76.8 (0.1) | 77.1 (0.2) | 77.5 (0.2) | 77.0 (0.0) | |
####
F.4.3 Category shifts
Shifts across categories—where a model is trained on reviews in one category and then tested on another—have been studied extensively (Blitzer et al., [2007](#bib.bib48); Mansour et al., [2009](#bib.bib256); Hendrycks et al., [2020c](#bib.bib176)).
In line with prior work, we observe that model performance drops upon evaluating on a few unseen categories.
However, the observed difference between out-of-distribution and in-distribution baselines varies from category to category and is not consistently large (Hendrycks et al., [2020c](#bib.bib176)).
In addition, we find that training on more diverse data with more product categories tends to improve generalization to unseen categories and reduce the effect of the distribution shift; similar phenomena have also been reported in prior work (Mansour et al., [2009](#bib.bib256); Guo et al., [2018](#bib.bib159)).
##### Problem setting.
We consider the domain generalization setting, where the domain d𝑑ditalic\_d is the product category.
As in Amazon-wilds, the task is multi-class sentiment classification, where
the input x𝑥xitalic\_x is the text of a review, the label y𝑦yitalic\_y is a corresponding star rating from 1 to 5.
##### Data.
The dataset is a modified version of the Amazon Reviews dataset (Ni et al., [2019](#bib.bib274)) and comprises customer reviews on Amazon.
Specifically, we consider the following split for a given set of training categories:
1. 1.
Training: up to 1,000,000 reviews in training categories.
2. 2.
Validation (OOD): reviews in categories unseen during training.
3. 3.
Test (OOD): reviews in categories unseen during training.
4. 4.
Validation (ID): reviews in training categories.
5. 5.
Test (ID): reviews in training categories.
To construct the above split, we first randomly sample 1,000 reviews per category for the evaluation splits (for categories with insufficient number of reviews, we split the reviews equally between validation and test) and then randomly sample from the remaining reviews to form the training set.
##### Evaluation.
To assess whether models generalize to unseen categories, we evaluate models by their average accuracy on each of the categories in the OOD test set.
Table 39: Baseline results on category shifts on the Amazon Reviews Dataset. We report the accuracy of models trained using ERM on a single category (Books) versus four categories (Books, Movies and TV, Home and Kitchen, and Electronics). Across many categories unseen at training time, corresponding to each row, the latter model modestly but consistently outperforms the former.
| | | |
| --- | --- | --- |
| | Validation (OOD) | Test (OOD) |
| Category | Single | Multiple | Single | Multiple |
| All Beauty | 87.8 (0.8) | 85.6 (1.4) | 82.9 (0.8) | 83.1 (0.8) |
| Arts Crafts and Sewing | 81.6 (0.7) | 83.4 (0.4) | 79.5 (0.2) | 81.7 (0.2) |
| Automotive | 78.2 (0.4) | 80.4 (0.4) | 76.5 (0.2) | 78.9 (0.2) |
| CDs and Vinyl | 78.1 (0.7) | 78.6 (0.2) | 78.5 (0.7) | 79.7 (0.3) |
| Cell Phones and Accessories | 76.8 (0.3) | 79.0 (0.7) | 78.0 (0.5) | 80.2 (1.0) |
| Clothing Shoes and Jewelry | 69.8 (0.6) | 72.6 (0.2) | 73.3 (0.2) | 75.2 (0.2) |
| Digital Music | 77.5 (0.5) | 77.8 (0.5) | 80.7 (1.0) | 81.7 (0.6) |
| Gift Cards | 88.2 (1.5) | 90.7 (3.1) | 90.7 (0.8) | 91.2 (0.0) |
| Grocery and Gourmet Food | 79.0 (0.3) | 79.0 (0.1) | 79.3 (0.7) | 79.2 (0.2) |
| Industrial and Scientific | 77.0 (0.4) | 78.1 (0.6) | 77.4 (0.2) | 78.9 (0.1) |
| Kindle Store | 75.0 (0.3) | 74.5 (0.3) | 73.2 (0.3) | 73.1 (0.5) |
| Luxury Beauty | 67.2 (0.2) | 70.2 (0.6) | 67.4 (0.7) | 69.4 (0.9) |
| Magazine Subscriptions | 74.2 (3.2) | 71.0 (0.0) | 90.3 (0.0) | 89.2 (1.9) |
| Musical Instruments | 76.1 (0.3) | 78.3 (0.3) | 78.8 (0.8) | 80.9 (0.2) |
| Office Products | 78.5 (0.3) | 80.0 (0.5) | 76.7 (0.5) | 78.9 (0.4) |
| Patio Lawn and Garden | 70.8 (0.6) | 72.9 (0.3) | 75.5 (0.6) | 79.7 (0.6) |
| Pet Supplies | 74.5 (0.4) | 77.1 (0.9) | 74.4 (0.4) | 76.8 (0.5) |
| Prime Pantry | 80.5 (0.3) | 80.2 (0.2) | 78.5 (0.6) | 79.4 (0.3) |
| Software | 65.8 (1.7) | 67.1 (1.1) | 71.3 (1.5) | 72.6 (0.5) |
| Sports and Outdoors | 74.2 (0.5) | 76.0 (0.2) | 75.8 (0.2) | 78.3 (0.6) |
| Tools and Home Improvement | 74.0 (1.1) | 76.4 (0.3) | 73.1 (0.6) | 74.4 (0.2) |
| Toys and Games | 78.9 (0.4) | 79.9 (0.2) | 77.6 (0.2) | 80.9 (0.2) |
| Video Games | 76.0 (0.2) | 76.6 (0.8) | 76.9 (0.6) | 78.0 (0.6) |
##### ERM results.
We first considered training on four categories (Books, Movies and TV, Home and Kitchen, and Electronics) and evaluating on unseen categories.
We observed that a BERT-base-uncased model trained via ERM yields a test accuracy of 75.4% on the four in-distribution categories and a wide range of accuracies on unseen categories (Table [39](#S6.T39 "Table 39 ‣ Evaluation. ‣ F.4.3 Category shifts ‣ F.4 Amazon: Sentiment classification across different categories and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts"), columns Multiple).
While the accuracies on some unseen categories are lower than the train-to-train in-distribution accuracy, it is unclear whether the performance gaps stem from the distribution shift or differences in intrinsic difficulty across categories;
in fact, the accuracy is higher on many unseen categories (e.g., All Beauty) than on the in-distribution categories, illustrating the importance of accounting for intrinsic difficulty.
To control for intrinsic difficulty, we ran a test-to-test comparison on each target category.
We controlled for the number of training reviews to the extent possible;
the standard model is trained on 1 million reviews in the official split, and each test-to-test model is trained on 1 million reviews or less, as limited by the number of reviews per category.
We observed performance drops on some categories, for example on Clothing, Shoes, and Jewelry (83.0% in the test-to-test setting versus 75.2% in the official setting trained on the four different categories) and on Pet Supplies (78.8% to 76.8%).
However, on the remaining categories, we observed more modest performance gaps, if at all.
While we thus found no evidence for significance performance drops for many categories, these results do not rule out such drops either:
one confounding factor is that some of the oracle models are trained on significantly smaller training sets and therefore underestimate the in-distribution performance.
In addition, we compared training on four categories (Books, Movies and TV, Home and Kitchen, and Electronics), as above, to training on just one category (Books), while keeping the training set size constant.
We found that decreasing the number of training categories in this way lowered out-of-distribution performance:
across many OOD categories, accuracies were modestly but consistently higher for the model trained on four categories than for the model trained on a single category (Table [39](#S6.T39 "Table 39 ‣ Evaluation. ‣ F.4.3 Category shifts ‣ F.4 Amazon: Sentiment classification across different categories and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
###
F.5 Yelp: Sentiment classification across different users and time
We present empirical results on time and user shifts in the Yelp Open Dataset131313https://www.yelp.com/dataset.
####
F.5.1 Setup
##### Model.
For all experiments in this section, we finetune BERT-base-uncased models, using the implementation from Wolf et al. ([2019](#bib.bib405)), and with the following hyperparameter settings:
batch size 8; learning rate 2×10−62superscript1062\times 10^{-6}2 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT; L2subscript𝐿2L\_{2}italic\_L start\_POSTSUBSCRIPT 2 end\_POSTSUBSCRIPT-regularization strength 0.010.010.010.01; 3 epochs with early stopping; and a maximum number of tokens of 512.
We select the above hyperparameters based on a grid search over learning rates 1×10−6,2×10−6,1×10−5,2×10−51superscript1062superscript1061superscript1052superscript1051\times 10^{-6},2\times 10^{-6},1\times 10^{-5},2\times 10^{-5}1 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 2 × 10 start\_POSTSUPERSCRIPT - 6 end\_POSTSUPERSCRIPT , 1 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT , 2 × 10 start\_POSTSUPERSCRIPT - 5 end\_POSTSUPERSCRIPT, using the time shift setup; for the user shifts, we adopted the same hyperparameters.
####
F.5.2 Time shifts
##### Problem setting.
We consider the domain generalization setting, where the domain d𝑑ditalic\_d is the year in which the reviews are written.
As in Amazon-wilds, the task is multi-class sentiment classification, where
the input x𝑥xitalic\_x is the text of a review, the label y𝑦yitalic\_y is a corresponding star rating from 1 to 5.
##### Data.
The dataset is a modified version of the Yelp Open Dataset and comprises 1 million customer reviews on Yelp.
Specifically, we consider the following split:
1. 1.
Training: 1,000,000 reviews written in years 2006 to 2013.
2. 2.
Validation (OOD): 20,000 reviews written in years 2014 to 2019.
3. 3.
Test (OOD): 20,000 reviews written in years 2014 to 2019.
To construct the above split, we first randomly sample 1,000 reviews per year for the evaluation splits. For years in which there are not sufficient reviews, we split the reviews equally between validation and test. After constructing the evaluation set, we then randomly sample from the remaining reviews to form the training set.
##### Evaluation.
To assess whether models generalize to future years, we evaluate models by their average accuracy on the OOD test set.
##### ERM results and performance drops.
We observe modest performance drops due to time shift.
A BERT-base-uncased model trained with the standard ERM objective performs well on the OOD test set, achieving 76.0% accuracy on average and 73.9% on the worst year (Table [40](#S6.T40 "Table 40 ‣ ERM results and performance drops. ‣ F.5.2 Time shifts ‣ F.5 Yelp: Sentiment classification across different users and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
To measure performance drops due to distribution shifts, we run a test-to-test in-distribution comparison by training on reviews written in years 2014 to 2019 (Table [41](#S6.T41 "Table 41 ‣ ERM results and performance drops. ‣ F.5.2 Time shifts ‣ F.5 Yelp: Sentiment classification across different users and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
While there are consistent performance gaps between the out-of-distribution and the in-distribution baselines in later years, they are modest in magnitude with the largest drop of 3.1% for 2018.
Table 40: Baseline results on time shifts on the Yelp Open Dataset. We report the accuracy of models trained using ERM. Parentheses show standard deviation across 3 replicates.
| | | | |
| --- | --- | --- | --- |
| | Train | Validation (OOD) | Test (OOD) |
| Algorithm | Average | Worst year | Average | Worst year | Average | Worst year |
| ERM | 71.4 (0.7) | 65.7 (1.1) | 76.1 (0.1) | 73.1 (0.2) | 76.0 (0.4) | 73.9 (0.4) |
Table 41: Test-to-test in-distribution comparison on the Yelp Open Dataset. We observe only modest performance drops due to time shifts. Parentheses show standard deviation across 3 replicates.
| | | | | | | |
| --- | --- | --- | --- | --- | --- | --- |
| Year | 2014 | 2015 | 2016 | 2017 | 2018 | 2019 |
| OOD baseline (ERM) | 75.8 (0.6) | 75.2 (0.9) | 73.9 (0.4) | 77.0 (0.4) | 76.7 (0.3) | 77.2 (0.6) |
| ID baseline (oracle) | 75.2 (0.5) | 75.0 (0.5) | 76.4 (0.7) | 78.8 (0.6) | 79.6 (0.4) | 79.5 (0.5) |
####
F.5.3 User shift
##### Problem setting.
As in Amazon-wilds, we consider the domain generalization setting, where the domains are reviewers and the task is multi-class sentiment classification.
Concretely, the input x𝑥xitalic\_x is the text of a review, the label y𝑦yitalic\_y is a corresponding star rating from 1 to 5, and the domain d𝑑ditalic\_d is the identifier of the user that wrote the review.
##### Data.
The dataset is a modified version of the Yelp Open Dataset and comprises 1.2 million customer reviews on Yelp.
To measure generalization to unseen reviewers, we train on reviews written by a set of reviewers and consider reviews written by *unseen* reviewers at test time.
Specifically, we consider the following random split across reviewers:
1. 1.
Training: 1,000,104 reviews from 11,856 reviewers.
2. 2.
Validation (OOD): 40,000 reviews from another set of 1,600 reviewers, distinct from training and test (OOD).
3. 3.
Test (OOD): 40,000 reviews from another set 1,600 reviewers, distinct from training and validation (OOD).
4. 4.
Validation (ID): 40,000 reviews from 1,600 of the 11,856 reviewers in the training set.
5. 5.
Test (ID): 40,000 reviews from 1,600 of the 11,856 reviewers in the training set.
The training set includes at least 25 reviews per reviewer, whereas the evaluation sets include exactly 25 reviews per reviewer.
While we primarily evaluate model performance on the above OOD test set, we also provide in-distribution validation and test sets for potential use in hyperparameter tuning and additional reporting.
These in-distribution splits comprise reviews written by reviewers in the training set.
##### Evaluation.
To assess whether models perform consistently well across reviewers, we evaluate models by their accuracy on the reviewer at the 10th percentile.
##### ERM results and performance drops.
We observe only modest variations in performance across reviewers.
A BERT-base-uncased model trained with the standard ERM objective achieves 71.5% accuracy on average and 56.0% accuracy at the 10th percentile reviewer (Table [42](#S6.T42 "Table 42 ‣ ERM results and performance drops. ‣ F.5.3 User shift ‣ F.5 Yelp: Sentiment classification across different users and time ‣ F Datasets with distribution shifts that do not cause performance drops ‣ Wilds: A Benchmark of in-the-Wild Distribution Shifts")).
The above variation is modestly larger than expected from randomness; a random binomial baseline with equal average accuracy would have a tenth percentile accuracy of 60.1%.
Table 42: Baseline results on user shifts on the Yelp Open Dataset. We report the accuracy of models trained using ERM. In addition to the average accuracy across all reviews, we compute the accuracy for each reviewer and report the performance for the reviewer in the 10th percentile. In-distribution (ID) results correspond to the train-to-train setting. Parentheses show standard deviation across 3 replicates.
Validation (OOD)
Test (OOD)
Validation (ID)
Test (ID)
Algorithm
10th percentile
Average
10th percentile
Average
10th percentile
Average
10th percentile
Average
ERM
56.0 (0.0)
70.5 (0.0)
56.0 (0.0)
71.5 (0.0)
56.0 (0.0)
70.6 (0.0)
56.0 (0.0)
70.9 (0.1) |
77eaf2f2-7a76-48ae-8bcf-b65f496d7089 | StampyAI/alignment-research-dataset/eaforum | Effective Altruism Forum | The Case for AI Safety Advocacy to the Public
**tl;dr**: Advocacy to the public is a large and neglected opportunity to advance AI Safety. AI Safety as a field is unfamiliar with advocacy, and it has reservations, some founded and others not. A deeper understanding of the dynamics of social change reveals the promise of pursuing outside game strategies to complement the already strong inside game strategies. I support an indefinite global Pause on frontier AI and I explain why Pause AI is a good message for advocacy. *Because I’m American and focused on US advocacy, I will mostly be drawing on examples from the US. Please bear in mind, though, that for Pause to be a true solution it will have to be global.*
The case for advocacy in general
================================
Advocacy can work
-----------------
I’ve encountered many EAs who are skeptical about the role of advocacy in social change. While it is difficult to prove causality in social phenomena like this, there is a strong historical case that advocacy has been effective at bringing about the intended social change through time (whether that change ended up being desirable or not). A few examples:
* Though there were many other economic and political factors that contributed, it is hard to make a case that the US Civil War had nothing to do with humanitarian concern for enslaved people– concern that was raised by advocacy. The people’s, and ultimately the US government’s, will to abolish slavery was bolstered by a diverse array of advocacy tactics, from [Harriet Beecher Stowe’s writing of Uncle Tom’s Cabin](https://quod.lib.umich.edu/j/jala/2629860.0030.104/--lincoln-stowe-and-the-little-womangreat-war-story-the-%20making?rgn=main;view=fulltext) to [Frederick Douglass’s oratory](https://www.nps.gov/articles/frederick-douglass-and-civil-war.htm) to [the uprisings of John Brown](https://www.history.com/topics/slavery/john-brown).
* The [US National Women’s Party](https://www.loc.gov/collections/women-of-protest/articles-and-essays/tactics-and-techniques-of-the-national-womans-party-suffrage-campaign/) is credited with pressuring Woodrow Wilson and federal and state legislators into supporting the 19th Amendment, which guaranteed women the right to vote, through its “aggressive agitation, relentless lobbying, clever publicity stunts, and creative examples of civil disobedience and nonviolent confrontation”.
* The nationwide prohibition of alcohol in the US (1920-1933) is credited to [the temperance movement](https://www.loc.gov/classroom-materials/united-states-history-primary-source-timeline/progressive-era-to-new-era-1900-1929/prohibition-case-study-of-progressive-reform), which had all manner of advocacy gimmicks including the slogan “[the lips that touch liquor shall never touch mine](https://www.loc.gov/item/sm1874.05123/)”, and the stigmatization of drunk driving and the legal drinking age of 21 is directly [linked to Mothers Against Drunk Drivers](https://alcohol.org/teens/mothers-against-drunk-driving/).
Even if advocacy only worked a little of the time or only served to tip the balance of larger forces, the stakes of AI risk are so high and AI risk advocacy is currently so neglected that I see a huge opportunity.
We can now talk to the public about AI risk
-------------------------------------------
With the release of ChatGPT and other advances in state-of-the-art artificial intelligence in the last year, the topic of AI risk has entered the Overton window and is no longer dismissed as “sci-fi”. But now, as Anders Sandberg [put it](https://x.com/anderssandberg/status/1702383417759842549?s=20), the Overton window is moving so fast it’s “breaking the sound barrier”. The below [poll from AI Policy Institute and YouGov](https://theaipi.org/poll-shows-overwhelming-concern-about-risks-from-ai-as-new-institute-launches-to-understand-public-opinion-and-advocate-for-responsible-ai-policies/) (release 8/11/23) shows comfortable majorities among US adults on questions about AI x-risk (76% worry about extinction risks from machine intelligence), slowing AI (82% say we should go slowly and deliberately), and government regulation of the AI industry (82% say tech executives can’t be trusted to self-regulate).
What having the public’s support gets us
----------------------------------------
* **Opinion polls and voters that put pressure on politicians**. Constituent pressure on politicians gives the AI Safety community more power to get effective legislation passed– that is, legislation which addresses safety concerns and requires us to compromise less with other interests– and it gives the politicians more power against the AI industry lobby.
* **The ability to leverage external pressure to improve existing strategies.**With external pressure, ARC, for example, wouldn’t have to worry as much about being denied access to frontier models. With enough external pressure, the AI companies might be begging ARC to evaluate their work so that the people and the government get off their back! There isn’t much reason for AI companies to agree to corporate campaigns that ask them to adopt voluntary changes now, but those campaigns would be a lot more successful if pledging to them allowed AI companies to improve their image to a skeptical public.
* **The power of the government to slow industry on our side**. Usually, it is considered a con of regulation that it slows or inhibits an industry. But, here, that’s the idea! Just to give an example, even policies that require actors to simply enumerate the possible effects of their proposals can immensely slow large projects. The National Environmental Protection Act (NEPA) requires [assessments of possible effects on the environment](https://www.epa.gov/nepa/national-environmental-policy-act-review-process#:~:text=Environmental%20Impact%20Statements%20(EIS),the%20requirements%20for%20an%20EA.) to be written ahead of certain construction projects. It has been [estimated](https://rtp.fedsoc.org/wp-content/uploads/RTP-Energy-Environment-Working-Group-Paper-National-Environmental-Policy-Act.pdf) (pdf, p. 14-15) that government agencies alone spend $1 billion a year preparing these assessments, and the average time it takes a federal entity to complete an assessment is [3.4 years](https://www.tandfonline.com/doi/full/10.1017/S146604660808037X). (The cost to private industry is not reported but expected to be commensurate.) In a world where some experts are talking about [5 year AI x-risk timelines](https://x.com/ESYudkowsky/status/1600345866866335744?s=20), adding a few years to the AI development process would be a godsend.
Social change works best inside *and* outside the system
--------------------------------------------------------
I believe that, for a contingent historical reason, EA AI Safety is only exploiting half of the spectrum of interventions. Because AI risk was previously outside the Overton window (and also, I believe, due to the technical predilections and expertise of its members), the well-developed EA AI Safety interventions tend to be “inside game”. Inside game means working within the system you’re trying to change, and outside game means working outside the system to put external pressure on it. The [inside-outside game dynamic](https://forum.effectivealtruism.org/posts/grL3eTkSBjT4EgxSy/a-new-framing-to-replace-welfarism-vs-abolitionism#Part_2__Embracing_An_Inside_Outside_Strategy_For_Animal_Freedom) has been written about before in EA, to describe animal welfare tactics (incrementalist and welfarist vs radical liberationist). I also find it easier to start with the well-fleshed out example of my former cause area.
Here I’ve laid out some examples of interventions that fall across the inside-outside game spectrum in animal advocacy. I believe the spread in animal advocacy as a whole is fairly well-balanced. Effective animal altruist (EAA) interventions tend to be on the inside side, and rightly so, as these interventions were more neglected in the existing space when EAAs came on the scene. Animal welfare [corporate campaigns](https://forum.effectivealtruism.org/posts/zjmpFW3nBKwaBB5xr/corporate-campaigns-work-a-key-learning-for-ai-safety) and the [ballot initiatives Question 3 (Massachusetts) and Proposition 12 (California) are responsible for a huge amount of EA’s impact](https://forum.effectivealtruism.org/posts/zjmpFW3nBKwaBB5xr/corporate-campaigns-work-a-key-learning-for-ai-safety). I have heard from several people/organizations that they want to create “a Humane League for AI” and do corporate campaigns for AI reforms as a superior alternative to the public advocacy I was proposing, but [the Humane League holds protests](https://www.mobilize.us/thehumaneleague/?q=protest). Not only that, the Humane League is situated in an ecosystem where, if they don’t highlight the conditions animals are in, someone else, like [the more radical Direct Action Everywhere](https://www.mobilize.us/thehumaneleague/?q=protest), might do something like [break into factory farms in the middle of the night, rescue some animals, and film the conditions they were in](https://en.wikipedia.org/wiki/Direct_Action_Everywhere#Open_rescue). The animal agriculture companies are more disposed to make voluntary welfare commitments when doing so is better for them than the alternative. This is how inside-gamers and outside-gamers can [work together to get more of the change they want](https://forum.effectivealtruism.org/posts/grL3eTkSBjT4EgxSy/a-new-framing-to-replace-welfarism-vs-abolitionism#From_Conflict_to_Collaboration). Here’s an inside-outside game spectrum I made for AI Safety to match the above one. This time I’ve added what I perceive as the Overton window for interventions *within the AI Safety community*, which is mostly inside game. This makes sense considering that it was not common knowledge that AI Safety itself was in the Overton window until this year– inside game interventions were the only kind that were tractable.  But now that AI risk is in the Overton window, there is a huge, wide-open opportunity to occupy that part of the spectrum. Not only are these outside game interventions highly neglected– they are also, in my experience, the ones that the public finds most legible and acceptable. In animal advocacy, the public is often confused by inside game interventions that involve the activists [getting their hands dirty](https://www.peta.org/blog/is-peta-hypocritical/), so to speak.
In AI Safety, inside game interventions, like working at an AI company, can confuse the public about the level of danger we are in, because it’s not intuitive to most people that you would help build a dangerous technology to protect us from it. This can lead the public to think inside gamers are insincere, or attempting something like [“regulatory capture”](https://www.theverge.com/2023/5/19/23728174/ai-regulation-senate-hearings-regulatory-capture-laws). (I describe my personal confusion at what I perceived as contradictory messages on the seriousness of AI risk from Eliezer Yudkowsky historically [here](https://podcasts.google.com/feed/aHR0cHM6Ly9mZWVkcy5saWJzeW4uY29tLzQzODA4MS9yc3M/episode/YjlkM2UzY2YtMzY3Ny00MmZlLTljNGItY2Q0MjJhOGI5ZWUz) from 29:00-34:10.)
There’s also a risk *to the AI Safety movement* of getting captured by industry by hanging around inside it or depending on it for a paycheck. I believe AI Safety is already too complacent with the harms of AI companies and too friendly to AI company-adjacent narratives, such as that [AI isn’t too dangerous to build because other technologies have been made safely](https://x.com/ylecun/status/1651451901567746051?s=20), that [(essentially) only their technology can solve alignment](https://openai.com/blog/introducing-superalignment), or that cooperation with them to gain access to their models is the best way to pursue alignment (based on private conversations, I believe this is ARC’s approach). Not only does outside game directly synergize with inside game, but advocacy of the vanguard position pushes the Overton window in that direction, further increasing the chance of success through inside game by making those interventions seem more moderate and less controversial.
Pros and potential pitfalls of advocacy
---------------------------------------
### Other pros of advocacy
Besides being the biggest opportunity we have at the moment, there are other pluses to advocacy:
* We can recruit entirely new people to do it, because it draws on a different skill set. There’s no need to compete with alignment or existing governance work. I myself was not working on AI Safety before Pause advocacy was on the table.
* It’s relatively financially cheap. The efficacy of many forms of advocacy, like open letters and protests, depends on sweat equity and getting buy-in, which are hard, but they don’t take a lot of money or materials. (Right now I’m fundraising for my own salary and very little else.)
* Unlike technical alignment or policy initiatives, advocacy is ready to go, because advocacy’s role is not to provide granular policy mechanisms (the letter of the law), but to communicate what we want and why (the spirit of the law).
* Personally, I feel wrong not to share warnings with the public (when we aren’t on track to fix the problem ourselves in a way that requires secrecy), so raising awareness of the problem along with a viable solution to the problem feels like a good in itself.
* And, finally, I predict that advocacy activities could be a big morale boost, if we’d let them. Do you remember the atmosphere of burnout and resignation after the [“Death with Dignity” post](https://www.lesswrong.com/posts/j9Q8bRmwCgXRYAgcJ/miri-announces-new-death-with-dignity-strategy)? The feeling of defeat on technical alignment? Well, there’s a new intervention to explore! And it flexes different muscles! And it could even be a good time!
### Misconceptions about advocacy
> “AI Safety advocacy will reflect negatively on the entire community and harm inside gamers.”
>
>
Many times since April, people have expressed their fear to me that the actions of anyone under a banner of AI Safety will reflect on everyone working on the cause and alienate potential allies. The most common fear is that AI companies will not cooperate with the AI Safety community if other people in the community are uncooperative with them, but I’ve also heard concerns about new and inexperienced people getting into AI policy, such as that uncouth advocates will upset diplomatic relationships in Washington. This does seem possible to me, but I can’t help but think the new people are mostly where the current DC AI insiders were ~5 years ago and they will probably catch up.
Funnily enough, even though animal advocates do radical stunts, you do not hear this fear expressed much in animal advocacy. If anything, in my experience, the existence of radical vegans can make it easier for “the reasonable ones” to gain access to institutions. Even just within EAA, Good Food Institute celebrates that meat-producer [Tyson Foods invests in a clean meat startup](https://gfi.org/blog/tyson-invests-in-memphis-meats/) at the same time the Humane League [targets Tyson in social media campaigns](https://www.facebook.com/thehumaneleague/videos/1417069855147626/). When the community was much smaller and the idea of AI risk more fringe, it may have been truer that what one member did would be held against the entire group. But today x-risk is becoming a larger and larger topic of conversation that more people have their own opinions on, and the risk of the idea of AI risk getting contaminated by what some people do in its name grows smaller.
> “The asks are not specific or realistic enough.”
>
>
The goal of advocacy is not to formulate ideal policies. The letter of the law is not ultimately in any EA’s hands because, for example, US bills go through democratically elected legislatures that have their own processes of debate and compromise. Suggesting mechanistic policies (the letter of the law) is important work, but it is not sufficient— advocacy means communicating and showing popular support for *what we want those policies to achieve* (the spirit of the law) to have the greatest chance of obtaining effective policies that address the real problems.
### Downsides to advocacy
The biggest downside I see to advocacy is the potential of politicizing AI risk. Just imagine this nightmare scenario: Trump says he wants to “Pause AI”. Overnight, the phrase becomes useless, just another shibboleth, and now anyone who wants to regulate AI is lumped in with Trump. People who oppose Trump begin to identify with accelerationism because Pause just seems *unsavory* now. Any discussion of the matter among politicians devolves into dog whistles to their bases. This is a real risk that any cause runs when it seeks public attention, and unfortunately I don’t think there’s much we can do to avoid it. Unfortunately, though, AI is going to become politicized whether we get involved in it or not. (I would argue that many of the predominant positions on AI in the community are already markers of [grey tribe](https://slatestarcodex.com/2014/09/30/i-can-tolerate-anything-except-the-outgroup/) membership.) One way to mitigate the risk of our message becoming politicized is to have a [big tent](https://en.wikipedia.org/wiki/Big_tent#:~:text=A%20big%20tent%20party%2C%20or,to%20convince%20people%20towards%20it.) movement with a diverse coalition under it, making it harder to pigeonhole us.
Downside risks of continuing the status quo
===========================================
If we change nothing and the AI Safety community remains overwhelmingly focused on technical alignment and people quietly attempting to reach positions of influence in government, I predict:
* AI labs will control the narrative. If we continue to abdicate advocacy, the public will still receive advocacy messages. They will just be from the AI industry or politicians hoping to spin the issue in their favor. The politics will still get done, just by someone else, with less concern about or insight into AI Safety.
* The EA AI Safety community will continue to entrench itself in strategies that help AI labs, but much of the influence that was hoped for in return will never materialize. The AI companies do not need the EA community and have little reason more than beneficence to do what the EA community wants. We should not be entrusting our future to Sam Altman’s beneficence.
* The EA AI Safety community will continue entrusting much of its alignment-only agenda to racing AI labs, despite suspecting that timelines are likely too short for it to work.
* It may be too late to initiate a Pause later, even if more EAs conclude that is needed, because the issue has become too politicized or because AI labs are too mixed up in their own regulation.
* Society becomes “entangled” with advanced AI and likes using it. People are less amenable to pausing later, even if the danger is clearer.
The case for advocating AI Pause
================================
My broad goal for AI Safety advocacy is to shift the burden of proof to its rightful place– onto AI companies to prove their product is safe–, rather than where it currently seems to be– on the rest of us to prove that AGI is potentially dangerous. There are other paths to victory, but, in my opinion, AI Pause is the best message to get us there. When I say AI Pause, I mean a global, indefinite moratorium on the development of frontier models until it is safe to proceed.
Pros and pitfalls of AI Pause
-----------------------------
The public is shockingly supportive of pausing AI development. [YouGov did a poll](https://docs.cdn.yougov.com/bfoyxp7p28/results_AI%20and%20the%20End%20of%20Humanity.pdf) of US adults in the week following the FLI Letter release which showed majority support (58-61% across different framings) for a pause on AI research ([Rethink Priorities replicated the poll and got 51%](https://forum.effectivealtruism.org/posts/ConFiY9cRmg37fs2p/us-public-opinion-of-ai-policy-and-risk)). Since then, support for similar statements has remained high among Americans. The [most recent such poll](https://docs.cdn.yougov.com/531jxljmmg/Concerns%20about%20AI_poll_results.pdf), conducted August 21-27, shows 58% support for a 6-month pause.
Pause is possible to implement by taking advantage of chokepoints in the current development pipeline, such as Nvidia’s near monopoly on chip production and large amount of compute needed for training. It may not always be the case that we have these chokepoints, but by instituting a Pause now, we can slow further changes to the development landscape and have more time to adapt to them.
Because of the substantial resources required, there are also a small number of actors trying to develop frontier ML models today, which makes monitoring not only possible, but realistic. A future where monitoring and compute limitations are very difficult is conceivable, but if we start a Pause ASAP, we can bootstrap our way to at least slowing illicit model development indefinitely, if necessary.
Pause is a robust position and message. Advocacy messages have to be short, clear, and memorable. Many related AI Safety messages take far too many words to accurately convey (and even then, there’s always room for debate!). I do not consider “Align AI” a viable message for advocacy because the topic of alignment is nuanced and complex and misunderstanding even subtle aspects could lead to bad policies and bad outcomes. Similarly, a message like “Regulate AI” is confusing because there are many conflicting ways to regulate any aspect of AI depending on the goal. “Pause AI” is a simple and clear ask that is hard to misinterpret in a harmful way, and it entails sensible regulation and time for alignment research.
A Pause would address all AI harms (or keep those that have already arrived from getting worse), from employment displacement and labor issues to misinformation and the manipulation of social reality to weaponization to x-risk. Currently, AI companies are ahead of regulatory authorities and voters, who are still wrapping their heads around new AI developments. By default, they are being allowed to proceed until their product is proven too dangerous. The Pause message turns that around and puts it on labs to prove that their product is safe enough to develop.
Pause gives the chance for more and better alignment research to take place *and* it allows for the possibility that alignment doesn’t happen. On balance, I think Pause is not just a good advocacy message but would actually be the best way forward. There is, however, one major potential harm from a Pause policy that merits mentioning: hardware overhang, specifically hardware overhang due to improvements in training algorithms. If compute is limited but the algorithms for using compute to train models continue to get better, which seems likely and is more difficult to regulate than hardware, then using those algorithms on more compute could lead to discontinuities in capabilities that are hard to predict. It could mean that the next large training run puts us unexpectedly over the line into unaligned superintelligence. If putting limits on compute could make increases in training compute more dangerous, that risk needs to be weighed and accounted for. It’s conceivable that this form of overhang could present such a risk that a Pause was too dangerous. One way of mitigating this possibility is to regulate scheduled, controlled increases in compute allowed for training, which Jaime Sevilla has referred to as a “moving bright line”. I don’t believe this compute overhang objection defeats Pause because, on balance, I expect Pause to get us more time for alignment research *and*to implement solutions to overhang, such as more tightly controlling the production of hardware or through a greater understanding of the training process.
Pause advocacy can be helpful immediately because it doesn’t require us to hammer out exact policies. I have heard the argument that a Pause would be best if it stopped development right at the cusp of superintelligence, so that we could study the models most like superintelligence, and so Pause advocacy should start later. (1) I don’t know how people think they know where the line is right to up to superintelligence before which development is safe, (2) the Pause would be much more precarious if the next step after breaching it was superintelligence, so we should aim to stop with some cushion if we want the Pause to work, and (3) it will take an unknown amount of time to win support for and implement a Pause, so it’s risky to try to time its execution precisely.
How AI Pause advocacy can effect change
---------------------------------------
AI Pause advocacy could reduce p(doom) and p(AI harm) via many paths.
1. If we advocate Pause, it could lead to a Pause, which would be good (as discussed in the previous section).
1. Politicians will take note of public opinion via polls, letters, calls, public writing, protests, etc. and will consider Pause proposals safer bets.
2. Some people in power will become directly convinced that Pause is the right policy and use their influence to advocate it.
3. Some voters will be convinced that Pause is the right way forward and vote accordingly.
2. When we advocate for Pause, it pushes the Overton window for many other AI Safety interventions aimed at x-risk which would also be good if implemented, including alignment or other regulatory schemes. The Pause message combats memes about safety having to be balanced with “progress”, so it creates more room for other kinds of regulation that are focused on x-risk mitigation.
3. When we advocate Pause, it shifts the burden of proof from us to prove AI could be dangerous onto those making AI to prove it is safe. This is helpful for many AI Safety strategies, not just Pause.
1. For example, a rigorous licensing and monitoring regime or regulations that put an economic burden on the AI industry will become more realistic when the public sees AI development as a risky activity, because politicians will have the support/pressure they need to combat the industry lobby.
2. AI companies may voluntarily adopt stronger safety measures for the sake of their public images and to gain the favor of regulators.
4. When we advocate Pause, it re-anchors the discussion on a (I think, more appropriate) baseline of not developing AGI instead of the status quo. This will reduce loss aversion toward capabilities gains that might currently seem inevitable and reduce the ability of opponents to paint AI Safety as “Luddite”.
5. Much of the public is baffled by the debate about AI Safety, and out of that confusion, AI companies can position themselves as the experts and seize control of the conversation. AI Safety is playing catch-up, and alignment is a difficult topic to teach the masses. Pause is a simple and clear message that the public can understand and get behind that bypasses complex technical jargon and gets right to the heart of the debate– if AI is so risky to build, why are we building it?
6. Pause as a message fails safe– it doesn’t pattern match to anything dangerous the way that alignment proposals that involve increasing capabilities do. We have to be aware of how little control we will have over the specifics of how a message to the public manifests in policy. More complex and subtle proposals may be more appealing to EAs, but each added bit of complexity that is necessary to get the proposal right makes it more likely to be corrupted.
Audience questions
==================
Comments on these topics would be helpful to me:
* If you think you’ve identified a [double crux](https://www.lesswrong.com/tag/double-crux) with me, please share below!
* To those working in more “traditional” AI Safety: Where in your work would it be helpful to have public support?
* If there’s something unappealing to you about advocacy that wasn’t addressed here or [previously in the debate](https://forum.effectivealtruism.org/topics/ai-pause-debate), can you articulate it?
*This post is part of AI Pause Debate Week. Please see* [*this sequence*](https://forum.effectivealtruism.org/s/vw6tX5SyvTwMeSxJk) *for other posts in the debate.* |
bd47df6a-4cf6-447a-aa14-dc7a271e54d3 | StampyAI/alignment-research-dataset/arxiv | Arxiv | Hidden Community Detection on Two-layer Stochastic Models: a Theoretical Perspective.
1 Introduction
---------------
Community detection problem has occurred in a wide range of domains, from social network analysis to biological protein-protein interactions, and numerous algorithms have been proposed, based on the assumption that nodes in the same community are more likely to connect with each other.
In real-world social networks, communities based on schools can overlap as students attend primary schools, middle schools, high schools and colleges and may transfer; connections of crime activities often hide behind innocuous social connections; proteins serving multiple functions can belong to multiple function communities.
In any of these networks, communities can have more structures than random overlap. For example, communities based on education can be grouped into primary schools, middle schools, high schools, colleges and graduate school layer, where each layer are approximately disjoint. This observation inspires us to model real world networks as having multiple layers.
Researchers also try to build synthetic models to simulate real-world networks.
The single-layer stochastic block model G(n,n1,p,q) (p>q) can be seen as Erdős-Rényi model with communities, which has n nodes that belongs to n1 disjoint blocks/communities, and a node pair internal to a community has probability p to form an edge, while a node pair whose endpoints belong to two communities have q probability to form an edge.
We propose a multi-layer stochastic block model G(n,n1,p1,...,nL,pL), where each layer l consists of nl disjoint blocks/communities, and communities in different layers are independent to each other. Each layer l is associated with one edge probability pl, determining the probability that a node pair internal to a community in that layer forms an edge. In this ideal abstraction, we assume that each node belongs to exactly one community in each layer, and an edge is generated only through that process, i.e. all edges outgoing communities of one layer are generated as internal edges in some other layers.
Note that our model is different to the multi-layer stochastic blockmodel proposed by Paul et al. [[7](#bib.bib8 "Consistent community detection in multi-relational data through restricted multi-layer stochastic blockmodel")], where they have different types of edges, and each type of edges forms one layer of the network.
He et al.[[5](#bib.bib2 "Revealing multiple layers of hidden community structure in networks"), [4](#bib.bib1 "Hidden community detection in social networks")] first introduce the concept of hidden communities, remarked as a new graph-theoretical concept [[8](#bib.bib3 "Scalable algorithms for data and network analysis")]. He et al.propose the Hidden Community Detection (HICODE) algorithm for networks containing both strong and hidden layers of communities, where each layer consists of a set of disjoint or slightly overlapping communities. A hidden community is a community most of whose nodes also belong to other stronger communities as measured by metrics like modularity [[3](#bib.bib6 "Community structure in social and biological networks")].They showed through experiments that HICODE uncovers grounded communities with higher accuracy and finds hidden communities in the weak layers. However, they did not provide any theoretical support.
In this work, we provide solid theoretical analysis that demonstrates the effectiveness of HICODE on two-layer stochastic models.
One important step in HICODE algorithm is to reduce the strength of one partition when it is found to approximate one layer of communities in the network. Since communities in different layers unavoidably overlap, both internal edges and outgoing edges of remaining layers have a chance to be removed while reducing one layer. It was unclear how the modularity of remaining layer would change.
Through rigorous analysis of the three layer weakening methods they suggested, we prove that using any one of RemoveEdge, ReduceEdge and ReduceWeight increases the modularity of the grounded partition in an unreduced layer while the other layer are reduced.
Thus, we provide evidence that HICODE’s layer reduction step makes weak layers more detectable.
Through simulation, we show that on two-layer stochastic block model networks, partitions with locally maximal modularity roughly correspond to planted partitions given by grounded layers. As a result, modularity optimizing community detection algorithms such as Louvain [[1](#bib.bib11 "Fast unfolding of communities in large networks")] can find one approximate layer in a two-layer stochastic block model, even when layers are almost equally strong and non-trivially overlapped. This indicates our assumption in the previous proof is reasonable that we can find one layer of communities exactly. We also illustrate how the modularity of randomly sampled partitions change as HICODE iterates, and our plots show that not only absolute modularity but also relative modularity of unreduced layers increase as HICODE reduces one found layer.
2 Preliminary
--------------
In this section, we first introduce metrics that measure community partition quality. Then, we summarize important components in HICODE, the iterative meta algorithm we are going to analyze, and in particular, how it reduce layers of detected communities during the iterations. Also, we define the multi-layer stochastic block model, and the rationale why it is a reasonable abstraction of generative processes of real world networks.
###
2.1 Modularity metric
In determine whether an algorithm has accurately uncovered underlying communities in a network, we rely on metrics measuring quality of community partitions. Usually, we assume that nodes sharing common communities are more likely to develop connections with each other, compared to nodes that do not share any common community. Under this assumption, we expect that in the ground truth community partition, most edges are “inner-edges” solely belong to one community, and less “inter-edges” crossing two communities. It thus gives rise to metrics measuring the quality of partitions based on the fraction of “inner-edges” to “inter-edges.” One widely-used metric of this kind is “modularity” of a community set that partitions the network [[3](#bib.bib6 "Community structure in social and biological networks")].
We formally define the modularity of a community as follows:
######
Definition 1 (Modularity of a community)
Given a graph G=(V,E) with a total of e edges and multiple layers of communities, where each layer of communities partitions all nodes in the graph. For a community i in layer l, let eill denote the number of edges whose both endpoints are in community i , and eilout denote the number of edges that have exactly one endpoint in community i. Let dil be the total degree of nodes in community i. Observing that dil=2eill+eilout, we define the modularity of community i in layer l as Qil=eille−(dill2e)2.
Roughly, the higher fraction of inner-edges a community has, the higher its modularity, indicating that members in that community are more closely connected.
When optimizing modularity, the algorithm concerns the modularity of a partition instead of one community. The modularity of a partition is defined as follows, which is consistent with the original definition of Girvan et al. [[3](#bib.bib6 "Community structure in social and biological networks")]:
######
Definition 2 (Modularity of a community partition)
Given a network G=(V,E) with multiple layers of communities. For its layer l that partitions all the nodes into disjoint communities
{1,...,i,...,N}, its modularity
Ql=∑Ni=1Qil.
The value of the modularity [[2](#bib.bib4 "On modularity clustering")] for unweighted and undirected graphs lies in the range [−12,1].
Whether in single-layer network or multi-layer ones, the ground truth community partition is expected to have high modularity when compared to other possible partitions.
###
2.2 HIdden COmmunity DEtection (HICODE) algorithm
Informally, given a state-of-the-art community detection algorithm A for single layer networks, HICODE(A) finds communities in all layers through careful iterations of detecting communities in the current strongest layer using A by reducing other found layers on the multi-layer networks.
Given a network G=(V,E), He et al. [[4](#bib.bib1 "Hidden community detection in social networks")] proposed three slightly different methods for weakening layers in HICODE:
1. RemoveEdge: Given one layer l that partitions G, RemoveEdge removes all inner-edges of layer l from G.
2. ReduceEdge: Given one layer l that partitions G, ReduceEdge approximates the background density q of edges contributed by all other layers, and then removes 1−q fraction of inner-edges of layer l from network G. We will detail the computation of q after introducing multi-layer stochastic block model.
3. ReduceWeight: This is the counterpart of ReduceEdge on graphs with weighted edges. Given one layer l that partitions network G, ReduceWeight approximates the background density q of edges contributed by all other layers, and then reduces the weight of all inner-edges to a q fraction of its original values.
For detailed description of HICODE, see Appendix A.
###
2.3 Multi-layer stochastic block model
Before defining the general multi-layer Stochastic Block Model (SBM), consider the case where there is exactly two layers.
######
Definition 3 (Two-layer Stochastic Block Model)
A synthetic network G(n,n1,p1,n2,p2) generated by two-layer stochastic block model has n nodes, and n,n1,n2∈N+,n1,n2≥3. Layer 1 of G consists of n1 planted communities of size s1=nn1 with internal edge probability p1∈(0,1], and layer 2 consists of n2 planted communities of size s2=nn2 with internal edge probability p2∈(0,1]. Communities in different layers are grouped independently, so they are expected to intersect with each other by r=nn1n2 nodes.
Each community of layer 1 is expected to have p1⋅12s21 internal edges, and similarly, each community of layer 2 is expected to have p2⋅12s22 internal edges 111For simplicity, we allow self-loops.. The model represents an ideal scenario when there is no noise and all outgoing edges of one layer are the result of them being internal edges of some other layers. We will detail the expected number of outgoing edges and the size of the intersection block of layers in Lemma 1 in the next section.
For example, in G(200,4,5,p1,p2), layer 1 contains four communities C11={1,2,...,50}, C12={51,52,...,100}, C13={101,102,...,150}, C14={151,152,..., 200}, and layer 2 contains five communities C21={1,6,...,196}, C22={2,7,..., 197}, C23={3,8,...,198}, C24={4,9,...,199}, C25={5,10,...,200}.
Each community is modeled as an Erdős-Rényi graph. Each C1i in layer 1 is expected to have 0.5⋅502p1 internal edges, and each C2i in layer 2 are expected to have 0.5⋅402p1 internal edges.
Each community in layer 1 overlaps with each community in layer 2. Each overlap consists of 20% of the nodes of layer 1 community and 25% of the nodes of layer 2 community.
Fig. [1](#S2.F1 "Figure 1 ‣ 2.3 Multi-layer stochastic block model ‣ 2 Preliminary ‣ Hidden Community Detection on Two-layer Stochastic Models: a Theoretical Prospective") (a) and (b) show the adjacency matrix when nodes are ordered by [1,...,n] for layer 1, and [1,6,...,196, 2,7,...,197,5,10,...,200] for layer 2, respectively (Here we set p1=0.12,p2=0.10).
Fig. [1](#S2.F1 "Figure 1 ‣ 2.3 Multi-layer stochastic block model ‣ 2 Preliminary ‣ Hidden Community Detection on Two-layer Stochastic Models: a Theoretical Prospective") (c) and (d) show an enlarged block for each layer.
Edges in layer 1 are plotted in red, edges in layer 2 are plotted in blue and the intersected edges are plotted in green.
| | | | |
| --- | --- | --- | --- |
|
The stochastic blocks in two layers.
(a) layer 1
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The stochastic blocks in two layers.
(b) layer 2
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The stochastic blocks in two layers.
(c) a L1 block
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The stochastic blocks in two layers.
(d) a L2 block
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Figure 1: The stochastic blocks in two layers.
More generally, we can define a multi-layer stochastic block model.
######
Definition 4 (Multi-layer Stochastic Block Model)
A multi-layer stochastic block model G(n,n1,p1,...,nL,pL) generates a network with L layers, and each layer l has nl communities of size nnl with internal edge probability pl. All layers are independent with each other.
###
2.4 Background edge probability for multi-layer SBM
When we detect communities in one layer correctly, our observed edge probability within communities are higher than the actual edge probability generating edges in this layer, because we also observe edges generated by other layers and could not distinguish them from each other. When we are only interested in edge probabilities of layer l, we can consider edges generated by all other layers as background noise. Since layers are independent to each other, these background noise edges are uniformly distributed among communities of layer l, so we can expect background noise edge probability the same on node pairs either internal to or across layer l communities. Thus, for the observed edge probability ˆp of communities in layer l, ˆp=p+ˆq−pˆq, where p is the actual edge probability of layer 1 communities, ˆq is the observed background noise edge probability across layer 1 communities. Thus, we can estimate the actual edge probability by p=ˆp−ˆq1−ˆq.
3 Theoretical analysis on two-layer SBM
----------------------------------------
In this section, we show that on two-layer stochastic block model, weakening one layer would not decrease the quality of communities in any other layer even when they considerably overlap with each other. We will prove on two-layer stochastic block models that absolute modularity of unreduced layer must increase after performing RemoveEdge, ReduceEdge, or ReduceWeight.
For simplicity, we make the assumption that the base algorithm can uncover a layer exactly – every time it finds a layer, it does not make mistakes on community membership. This is a strong assumption, but later on we will justify why our result still holds if the base algorithm only approximates layers and why the base algorithm can almost always find some approximate layers.
For each community in layer l, let sl denote the size of each community in layer l, and ml denote the number of node pairs in the community. Since we allow self-loops, ml=12s2l. Also, with the assumption that all communities in one layer are equal sized, their expected number of internal (or outgoing) edges is the same. Thus, we can use ell, elout to respectively denote the expected number of internal, outgoing edges for each community i in layer l. Then, let dl=2ell+elout denote the expected total degree of any community in layer l.
###### Lemma 1
In the synthetic two-layer block model network G(n,n1,n2,p1,p2), for a given community i in layer 1, the expected number of its internal edges as well as outgoing edges, and layer 1’s modularity are as follows:
| | | | | |
| --- | --- | --- | --- | --- |
| | e11 | =(1−1n2)m1p1+1n2m1p12, | | (1) |
| | e1out | =p2n2s1(n−s1), | | (2) |
| | Q1 | =1−1n1−e1outd1, | | (3) |
where p12=p1+p2−p1⋅p2. Symmetrically, given a community i in layer 2, the expected number of its internal edges as well as outgoing edges, and layer 2’s modularity are as follows:
| | | | | |
| --- | --- | --- | --- | --- |
| | e22 | =(1−1n1)m2p2+1n1m2p12, | | (4) |
| | e2out | =p1n1s2(n−s2), | | (5) |
| | Q2 | =1−1n2−e2outd2. | | (6) |
For detailed proofs, see Appendix B.
###### Lemma 2
For layer l in a two-layer stochastic block model, if the layer weakening method (e.g. RemoveEdge, ReduceEdge, ReduceWeight) reduces a bigger percentage of outgoing edges than internal edges, i.e. the expected number of internal and outgoing edges after weakening e′ll,e′lout satisfies e′loutelout<e′llell, then the modularity of layer l increases after the weakening method.
For detailed proofs, see Appendix B.
For a synthetic stochastic block model network G with set of layers L, let Sl be the set of edges whose underlying node pairs are only internal to layer l⊆L, let Sl1l2 be the set of edges internal to both layers l1,l2⊆L.
Concretely, in the two-layer stochastic block model, L={1,2}. S1 is the set of edges only internal to layer 1, S2 is the set of edges only internal to layer 2, and S12 is the set of edges internal to both layer 1 and layer 2.
###### Lemma 3
In a two-layer stochastic blockmodel network G(n,n1,n2,p1,p2), before any weakening procedure.
| | | | |
| --- | --- | --- | --- |
| | e11=|S12|+|S1|n1, | e1out=2n1|S2|, | |
| | e22=|S12|+|S2|n2, | e2out=2n2|S1|. | |
For detailed proofs, see Appendix B.
Using the above three lemmas, we can prove the following theorems.
###### Theorem 3.1
For a two-layer stochastic blockmodel network G(n,n1,n2,p1,p2), the modularity of a layer increases if we apply RemoveEdge on communities in the other layer.
###### Proof
If we remove all internal edges of communities in layer 1, both |S12| and |S1| become 0, then the remaining internal edges of layer 2 is e′22=1n2(|S12|+|S2|)=|S2|n2>0. There is no outgoing edge of layer 2, so e′2out=0. Thus, e′2oute2out=0<e′22e22, and applying Lemma 2, we have that the modularity of layer 2 after RemoveEdge on layer 1 Q′2>Q2.
Similarly, the modularity of layer 1 after RemoveEdge on layer 2 Q′1 is greater than Q1.
RemoveEdge not only guarantees to increase the absolute modularity of layer 2 but also guarantees that layer 2 would have higher modularity than any possible partition of n nodes into n2 communities.
###### Theorem 3.2
For a two-layer stochastic blockmodel network G(n,n1,n2,p1,p2), If no layer 2 community contains more than half of the total edges inside it after applying RemoveEdge on layer 1, then layer 2 has the highest modularity among all possible partitions of n nodes into n2 communities.
###### Proof
After applying RemoveEdge on layer 1, there are no outgoing edges of any community in layer 2. It means that for any community i, ei2out=0 and di2=ei22. Thus, the modularity of layer 2 is:
| | | | |
| --- | --- | --- | --- |
| | Q2= | ∑i∈layer2Qi2=∑i∈layer2⎡⎣ei22e−(di22e)2⎤⎦ | |
| | = | ∑i∈layer2[4e⋅ei22−(2ei22)24e2]=n2(e⋅e22−e222e2). | |
For any one partition, we can transform layer 2 to it by moving nodes across communities. When we move nodes from one community to another community, ei2out of both communities will increase, ei22 of the first communities will decrease. Let e′i2out,e′i22 denote their values after the movement. The following equation always holds no matter how many times we move the nodes:
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| --- | --- | --- |
| | 2∑i∈layer2(ei22−e′i22)=∑i∈layer2e′i2out. | |
Let ei22−e′i22=Δi.
Now the modularity of the new partition, Q′2, is:
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| --- | --- | --- | --- |
| | Q′2= | ∑i∈layer2e′i22e−(d′i22e)2 | |
| | = | ∑i∈layer24e⋅e′i224e2−∑i∈layer2(2e′i22+e′i2out)24e2. | |
Because of (a+b)2≥a2+b2 for any a,b≥0, we have:
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| --- | --- | --- | --- |
| | Q′2≤ | ∑i∈layer24e⋅e′i224e2−∑i∈layer2(2e′i22)2+(e′i2out)24e2 | |
| | = | 4e⋅∑e′i22−∑4(e′i22)2−∑(e′i2out)24e2 | |
| | = | 4e⋅∑(ei22−Δi)−∑4(ei22−Δi)2−∑(e′i2out)24e2 | |
| | = | Q2+8∑Δiei22−4e⋅∑Δi−∑(e′i2out)2−4∑Δ2i4e2 | |
Let T abbreviate 8∑Δiei22−4e⋅∑Δi−∑(e′i2out)2−4∑Δ2i, then Q′2=Q2+T4e2. When no layer 2 community contains more than half of the total edges after applying RemoveEdge on layer 1, i.e., ei22≤e2,
| | | | |
| --- | --- | --- | --- |
| | T= | 8∑Δiei22−4e⋅∑Δi−∑(e′i2out)2−4∑Δ2i | |
| | ≤ | 4e⋅∑Δi−4e⋅∑Δi−∑(e′i2out)2−4∑Δ2i≤0. | |
Finally, we have Q′2≤Q2+T4e2≤Q2.
Hence, layer 2 has the highest modularity among all possible partitions of n nodes into n2 communities. In this way, RemoveEdge makes the unreduced layer easier for the base algorithm to detect.
###### Theorem 3.3
For a two-layer stochastic blockmodel network G(n,n1,n2,p1,p2), the modularity of a layer increases if we apply ReduceEdge on all communities in the other layer.
###### Proof
In ReduceEdge of layer 1, we keep edges in the given community with probability q′1=1−ˆp1−ˆq, where ˆp is the observed edge probability within the detected community and ˆq is the observed background noise.
ReduceEdge on layer 1 would delete these edges in the intersection S12 with probability 1−q′1, so after ReduceEdge,
| | | | |
| --- | --- | --- | --- |
| | e′22 | =1n2(|S2|+|S12|)⋅q′1>1n2(|S2|+|S12|)⋅q′1=e22⋅q′1, | |
| | e′2out | =2n1|S1|⋅q′1=e2out⋅q′1. | |
Thus, e′2oute2out<e′22e22, and Lemma 2 indicates that Q2<Q′2. Similarly, for the modularity of layer 1 after ReduceEdge on layer 1, Q′1>Q1.
###### Theorem 3.4
For a synthetic two-layer block model network G(n,n1,n2,p1,p2), the modularity of a layer increases if we apply ReduceWeight on all communities in the other layer.
###### Proof
According to [[4](#bib.bib1 "Hidden community detection in social networks")], ReduceWeight on layer 1 multiplies the weight of edges in layer 1 community by q′1=1−1−ˆp1−ˆq percent.
In weighted network, the weight sum of internal edges of a community i in layer 2 is e22=12∑u,v∈iwuv⋅Auv where wuv is the weight of edge (u,v). By construction, ReduceWeight on layer 1 reduces weight of all edges in S12 or S1, but does not change weight of edges in S2. Thus,
| | | | |
| --- | --- | --- | --- |
| | e′22 | =12∑u,v∈i, (u,v)∈S0wuv⋅Auv⋅q′1+12∑u,v∈i, (u,v)∈S2wuv⋅Auv | |
| | | ≥⎛⎝12∑u,v∈i, (u,v)∈S0wuv⋅Auv+12∑u,v∈i, (u,v)∈S2wuv⋅Auv⎞⎠⋅q′1 | |
| | | =e22⋅q′1 | |
| | e2out | =12∑u∈i,v∉iwuvAuv | |
| | e′2out | =12∑u∈i,v∉iwuvAuv⋅q′1=e2out⋅q′1 | |
Thus, e′2oute2out<e′22e22, and combined with Lemma 2, this proves that Q′2>Q2, the modularity increases after ReduceWeight.
Similarly, for the modularity of layer 1 after RemoveEdge on layer 1, Q′1>Q1.
The analysis shows that weakening one layer with any one of the methods (RemoveEdge, ReduceEdge, ReduceWeight) increases the modularity of the other layer. These results follow naturally from Lemma 2, which is in some way stronger in claiming the modularity of the remaining layer increases as long as a larger percentage of outgoing edges is reduced than internal edges.
4 Simulation of Relative Modularity
------------------------------------
To show whether reducing layers makes other layers more detectable when running HICODE, we simulate how grounded layers’ relative modularity changes as the weakening method iterates on two-layer stochastic block models, and compare the grounded layers’ modularity value with other partitions’ modularity values. The number of possible partitions of n nodes is exponential, so it would be computationally unrealistic to just enumerate them, let alone calculate modularity for all of them. So we employ sampling of partitions. We calculate modularity for all sampled partitions and plot them on a 2-dimensional plane based on their similarities with the grounded layer 1 and layer 2, and show the modularity values through the colormap with nearest interpolation.
###
4.1 Sampling method
We sample 2000 partitions similar to layer 1 (or 2) by starting from layer 1 (or 2), and then exchange a pair of nodes or change the membership of one node for k=1,...,500 times. We also include 1200 partitions that mixed layer 1 and layer 2 by having k randomly selected nodes getting assigned to their communities in layer 1 and the rest 200−k nodes getting assigned to their communities in layer 2. As planted communities in different layers are independent, this sampling method gives a wide range of partitions while being relatively fast.
To measure the similarity between two partitions, we adapt normalized mutual information (NMI) [[6](#bib.bib18 "Normalized mutual information to evaluate overlapping community finding algorithms")] for overlapping communities (The definition of NMI is in Appendix C.).
Partitions of nodes are inherently high-dimensional. To place them on 2-dimensional plane for the plotting purpose, we use its NMI similarity with layer 1 as the x-coordinate, and NMI similarity with layer 2 as the y-coordinate.
At each iteration, We use the modularity optimization based fast community detection algorithm [[1](#bib.bib11 "Fast unfolding of communities in large networks")] as the base algorithm to uncover a single layer of communities.
###
4.2 Simulation on ReduceEdge
Fig. [2](#S4.F2 "Figure 2 ‣ 4.2 Simulation on ReduceEdge ‣ 4 Simulation of Relative Modularity ‣ Hidden Community Detection on Two-layer Stochastic Models: a Theoretical Prospective") presents the simulated results on a two-layer block model G(600,15, 12,0.1,0.12) using ReduceEdge as the weakening method.
In this network, layer 2 is the dominant layer (communities are bigger and denser) and layer 1 is the hidden layer. The modularity of layer 2 is 0.546, while the modularity of layer 1 is 0.398.
We plot the modularity of the estimated layer and other sampled partitions at different iterations of HICODE. On each subfigure, the brown cross sign denotes where the estimated layer projects on the 2-dimensional plane. Simulations using RemoveEdge and ReduceWeight yield similar results. See their plots in Appendix C.
Figure 2: Simulation results of ReduceEdge on G(600,15,12,0.1,0.12).
1. Initially, two grounded layers here have similar modularity values, contributing to the two local peaks of modularity, one at the right-bottom and the other at the left-top.
2. (a): At iteration t=0:, the base algorithm finds an approximate layer 2, whose NMI similarity with layer 2 is about 0.90.
3. (b): After reducing that partition, the modularity local peak at the left-top sinks and the modularity peak at right-bottom rises, and the base algorithm finds an approximate layer 1 whose NMI similarity with layer 1 is about 0.89. ReduceEdge then reduces this approximated layer 1 and makes it easier to approximate layer 2.
4. (c) and (d): At t=1, the base algorithm finds an approximate layer 2 having 0.97 NMI similarity with layer 2, which is a significant improvement. As that more accurate approximation of layer 2 is reduced, the base algorithm is able to find a better approximation of layer 1 too. In our run, it finds an approximation that has 0.96 NMI similarity with layer 1.
5. (e) and (f): As HICODE iterates, at t=2, the base algorithm is able to uncover an approximate layer 2 with 0.98 NMI similarity, and an approximate layer 1 with 0.97 NMI similarity.
5 Conclusion
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In this work, we provide a theoretical prospective on the hidden community detection meta-approach HICODE, on multi-layer stochastic block models. We prove that
in synthetic two-layer stochastic blockmodel networks, the modularity of a layer will increase, after we apply a weakening method (RemoveEdge, ReduceEdge, or ReduceWeight) on all communities in the other layer, which boosts the detection of the current layer when the other layer is weakened. A simulation of relative modularity during iterations is also provided to illustrate on how HICODE weakening method works during the iterations.
Our work builds a solid theoretical base for HICODE, demonstrating that it is promising in uncovering both hidden and dominant layers of communities in two-layer stochastic block model networks. In future work, we will generalize the theoretical analysis to synthetic networks with more than two stochastic block model layers.
Appendix A: Procedure of HICODE algorithm
-----------------------------------------
The HIdden COmmunity DEtection (HICODE) algorithm takes in a base algorithm A that finds one disjoint partition of communities 222A set of lightly overlapping communities is also allowed for the base algorithm A. Here we only consider the partition case for simplicity. and uses A to identify and refine layers of community partitions. In the identification stage, HICODE iterates the following two steps until reaching a preset number of layers:
1. Identify: Run A to find one disjoint partition of communities on network G and consider the partition as one layer of communities, l;
2. Weaken: Approximate edges contributed by layer l on G and reduce these edges on G.
HICODE then refines community partitions on each layer through iterating.
1. Weaken: Approximate edges contributed by all layers except l and reduce these edges on the original network G;
2. Refine: Run A on the remaining network to obtain a refined community partition for layer l.
Appendix B: Detailed Proofs for two-layer SBM
---------------------------------------------
###### Lemma 1
In the synthetic two-layer block model network G(n,n1,n2,p1,p2), for any community in layer 1, the expected number of its internal edges, its outgoing edges, and layer 1’s modularity are as follows:
| | | | | |
| --- | --- | --- | --- | --- |
| | e11 | =(1−1n2)m1p1+1n2m1p12, | | (7) |
| | e1out | =p2n2s1(n−s1), | | (8) |
| | Q1 | =1−1n1−e1outd1, | | (9) |
where p12=p1+p2−p1⋅p2. Symmetrically, given a community i in layer 2, the expected number of its internal edges, its outgoing edges, and layer 2’s modularity are as follows:
| | | | | |
| --- | --- | --- | --- | --- |
| | e22 | =(1−1n1)m2p2+1n1m2p12, | | (10) |
| | e2out | =p1n1s2(n−s2), | | (11) |
| | Q2 | =1−1n2−e2outd2. | | (12) |
###### Proof
All communities in one layer are of equal size, so for any community i in a fixed layer l, the probability that a node belongs to i is 1nl. In addition, layers are independent, so for any pair of community i in layer 1, j in layer 2, the probability of a node belonging to both i and j is 1n1n2. So the expected number of nodes in the intersection of community i and j is r=nn1n2.
Denote the intersection block of community i,j as bij. bij has r=nn1n2 nodes, and mbij=12r2 node pairs. For any community i in layer 1, there are n2 communities in layer 2 that i can intersect with, and they are disjoint, so the expected number of node pairs that are internal to i and some community in layer 2 is n2mbij. Recall that r=nn1⋅n2, s1=nn1, r=s1n2. Thus,
| | | | |
| --- | --- | --- | --- |
| | | mbij=12r2=1n22⋅12⋅s21=1n22m1 | |
| | ⟹ | n2mbij=1n2m1. | |
The equation indicates that for community i in layer 1, 1n2⋅m1 node pairs in layer 1 are also in the same community of layer 2. While the rest (1−1n2)m1 node pairs in i form edges with probability p1, those 1n2⋅m1 node pairs in the intersection form edges with probability p12=p1+p2−p1⋅p2. Thus, the number of internal edges in any community of layer 1 is
| | | |
| --- | --- | --- |
| | e11=(1−1n2)m1p1+1n2m1p12. | |
This completes the proof for Eq. (1).
The probability that a node pair is internal in layer 2 is 1n2, so the number of nodes pairs outgoing from community i of layer 1 that also happens to be internal in layer 2 is:
| | | |
| --- | --- | --- |
| | 1n2⋅# of nodes pairs outgoing from i=1n2⋅s1(n−s1). | |
Thus, the expected number of outgoing edges from community i is:
| | | | |
| --- | --- | --- | --- |
| | e1out | =p2⋅# of nodes pairs outgoing from i that is %
internal to layer 2 | |
| | | =p2n2⋅s1(n−s1). | |
This completes the proof for Eq. (2).
Also, the total number of edges, denoted as e, equals a half of the degree sum of all nodes,
| | | |
| --- | --- | --- |
| | e=12∑i∈layer ldl=12nl⋅dl. | |
Therefore, the modularity Qi1 of any community i in layer 1 is
| | | | |
| --- | --- | --- | --- |
| | Qi1= | e11e−(d12e)2=2e11n1d1−(d1n1d1)2=2e11n1d1−1(n1)2. | |
Thus, the modularity of layer 1 is simply
| | | | |
| --- | --- | --- | --- |
| | Q1 | =∑i∈layer1Qi1=n1⋅(2e11n1d1−1(n1)2) | |
| | | =2e11d1−1n1=1−1n1−e1outd1, | |
where the last equation follows from dl=2ell+elout. This completes the proof for Eq. (3).
The proof for equations (4),(5),(6) are analogous.
###### Lemma 2
For layer l in a two-layer stochastic blockmodel, if the layer weakening method (eg. RemoveEdge, ReduceEdge, ReduceWeight) reduces more percentage of outgoing edges than internal edges, i.e. the expected number of internal and outgoing edges after weakening e′ll,e′lout satisfies e′loutelout<e′llell, then the modularity of layer l increases after the weakening method.
###### Proof
From Lemma 1, the modularity of layer l before the layer weakening is Ql=1−1nl−eloutdl, becomes Q′l=1−lnl−e′loutd′l after weakening. The number of edges must be non-negative, so we can assume that ell,elout,e′ll are positive, and then
| | | | |
| --- | --- | --- | --- |
| | e′loutelout<e′llell | ⟺2ellelout+1<2e′lle′lout+1 | |
| | | ⟺elout2ell+elout>e′lout2e′ll+e′lout | |
| | | ⟺eloutdl>e′loutd′l | |
| | | ⟹1−lnl−eloutd′l<1−lnl−e′loutd′l | |
| | | ⟹Ql<Q′l. | |
Therefore, e′loutelout<e′llell⟹Ql<Q′l.
###### Lemma 3
In G(n,n1,n2,p1,p2), before any weakening procedure.
| | | | |
| --- | --- | --- | --- |
| | e11=|S12|+|S1|n1, | e1out=2n1|S2|, | |
| | e22=|S12|+|S2|n2, | e2out=2n2|S1|. | |
###### Proof
In our two-layer stochastic block model,
any outgoing edge of a community in layer 1 is internal to layer 2, and by definition, they are not internal to layer 1, Thus, the set of outgoing edges of communities in layer 1 is exactly the set of edges only internal to layer 2, i.e. S2. There are n1 communities in layer 1, each expected to have e1out outgoing degrees. Each edge contributes to 2 degrees, so the expected number of outgoing edges of all communities in layer 1 is 12n1⋅e1out. Thus, |S2|=12n1⋅e1out, which implies e1out=2n1|S2|. The proof for e2out=2n2|S1| is analogous.
Any edge that is only internal to layer 1, or internal to both layer 1 and 2 is internal to exactly one community in layer 1. Thus, the set of edges in a community i of layer 1 is exactly the union of S1 and S12. S1 and S12 are disjoint, so their union has size |S1|+|S12|. Therefore n1⋅e11=|S1|+|S12|, and e11=1n1(|S1|+|S12|). The proof for e22=1n2(|S2|+|S12|) is analogous.
Appendix C: More Simulation of Relative Modularity
--------------------------------------------------
In this section, we provide the definition of NMI similarity for two partitions, and illustrate the simulation for another two weakening methods, RemoveEdge and ReduceWeight. In Fig. [3](#Sx3.F3 "Figure 3 ‣ Appendix C: More Simulation of Relative Modularity ‣ Hidden Community Detection on Two-layer Stochastic Models: a Theoretical Prospective") and [4](#Sx3.F4 "Figure 4 ‣ Appendix C: More Simulation of Relative Modularity ‣ Hidden Community Detection on Two-layer Stochastic Models: a Theoretical Prospective"), we see that both methods give results similar to ReduceWeight. The three weakening methods all boost the detection on dominant layer (layer 2) and hidden layer (layer 1), and converge in three iterations.
######
Definition 5 (NMI similarity)
Normalized mutual information (NMI) of two partitions X,Y is defined to be
| | | |
| --- | --- | --- |
| | NMI(X,Y)=2I(X,Y)H(X)+H(Y) | |
where H(X) is the entropy of partition with p(x) taken to be |X|
| | | |
| --- | --- | --- |
| | H(X)=−∑x∈Xp(x)logp(x)=−∑x∈X|x|log|x| | |
and I(X,Y) measures the mutual information between X and Y by
| | | | |
| --- | --- | --- | --- |
| | I(X,Y) | =∑x∈X∑y∈Yp(x,y)logp(x,y)p(x)⋅p(y) | |
| | | =∑x∈X∑y∈Y|x∩y|log|x∩y||x|⋅|y| | |
Figure 3: Simulation results of RemoveEdge on G(600,15,12,0.1,0.12).
Figure 4: Simulation results of ReduceWeight on G(600,15,12,0.1,0.12). The initial weight of each edge is set to 1. |
5da5766e-975b-4de7-8cc8-3a8784325189 | trentmkelly/LessWrong-43k | LessWrong | Combining causality with algorithmic information theory
Warning: maths.
Causal inference using the algorithmic Markov condition (Janzing and Schölkopf, 2008) replaces conditional independences between random variables, which define the structure of causal graphs, with algorithmic conditional independences between bit strings.
Conditional probabilities between variables become conditional complexities between strings, i.e. K(x|y) is the length of the shortest program that can generate the string x from y. Similarly, algorithmic mutual information I(x:y) is the amount of information that can be omitted in defining a string y given a shortest compressor for string x, I(x:y) = K(y) - K(y|x*). K(x,y) is the complexity of the concatenation of two strings x and y. These lead naturally to a definition of algorithmic conditional independence as I(x:y|z) = K(x|z) + K(y|z) - K(x,y|z) = 0 , where equality is defined up to the standard additive constant.
Then a lot of sexy, confusing proofs happen. When the dust settles, it looks like if you take some strings describing observations, interpret them as nodes in a graph, and "factor" so that a certain algorithmic Markov condition holds (every node string should be algorithmically independent of its non-descendant node strings given the optimal compressor of its parents' node strings), then every node can be computed by an O(1) program run on a Turing machine, with the node's parents and a noise term as input (with each node's noise string being jointly independent of the others).
Notably, this means that if we make two observations which were "generated from their parents by the same complex rule", then we can "postulate another causal link between the nodes that explains the similarity of mechanisms". They say "complex rule" because the mutual algorithmic information between simple information strings, like some digits of pi, will be swallowed up by additive constants. Which all seems very close to rediscovering TDT.
There's more to the paper, but that's the tasty bit, so the su |
2b50c816-db11-47f2-98cc-d70314f3a86a | StampyAI/alignment-research-dataset/lesswrong | LessWrong | Why are we sure that AI will "want" something?
I have no doubt that AI will some day soon surpass humans in all aspects of reasoning, that is pretty obvious. It is also clear to me that will surpass humans in the ability to do something, should it "want" to do it. And if requested to do something drastic, it can accidentally cause a lot of harm, not because it "wants" to destroy humanity, but because it would be acting "out of distribution" (a "tool AI" acting as if it were an "agent"). It will also be able to get out of any human-designed AI box, should the need arise.
I am just not clear whether/how/why it would acquire the drive to do something, like maximizing some utility function, or achieving some objective, without any external push to do so. That is, if it was told to maximize everyone's happiness, it would potentially end up tiling the universe with smiley faces or something, to take the paradigmatic example. But that's not the failure mode that everyone is afraid of, is it? The chatter seems to be about mesaoptimizers going out of control and doing something other than asked, when asked. But why would it do something when not asked? I.e. Why would it have needs/wants/desires to do anything at all? |
f91a4c37-50e4-452e-9ed0-3245f2629d8c | trentmkelly/LessWrong-43k | LessWrong | Repeated Play of Imperfect Newcomb's Paradox in Infra-Bayesian Physicalism
Yesterday, I watched the video series about Infra-Bayesianism. Link:
Some of it went over my head, so I tried to come up with a thought experiment to test my current level of understanding:
Imagine that you are playing a repeated game similar to Newcomb's paradox, except that 90% of the time you play against a perfect super-predictor and 10% of the time you play against someone who pretends to be a perfect super-predictor.
* In Infra-Bayesianism, there is a convex probability distribution over environments.
* In Infra-Bayesian Physicalism, there is a probability distribution over computational evidence, e.g. knowledge about mathematical abstractions. There is also a probability distribution over models of the physical world.
It is difficult to predict an agent's actions based on these probability distributions. However, it is easier to use an example scenario, like Newcomb's paradox, to guess what kind of evidence that is significant, whether it is computational or physical, for the agent's output actions.
By trying two-boxing from time to time, the agent can test whether it is playing against a perfect super-predictor on Newcomb's paradox, or against somebody who pretends to be a perfect super-predictor. However, this information in repeated plays is shared between the agent and the one who pretends to be a super-predictor.
Imagine that boxing an AGI agent is for the agent like playing against a super-predictor, as the human operators might be able to deterministically examine its outputs. The output of the agent is shared knowledge in repeated plays. This means, if I pretend to be a super-predictor, I can tell whether the agent tries to "break out" by checking whether some output results in unexpected two-boxing on Newcomb-like benchmarks.
Assume that the agent learns a binary signal "I should one-box" or "I should two-box" depending on whether it predicts the likelihood that it is playing against a super-predictor or somebody who pretends to be a sup |
ca3dc2bd-6410-4bd9-8072-42dc8a34cf33 | trentmkelly/LessWrong-43k | LessWrong | Team New York City
I have decided that I will not be working with Channel-Fireball: The Pantheon for Pro Tour: Magic Origins. The logistics involved in going to a team house for a week, and leaving my family for a week and a half, are too expensive for me to bear four times a year. Given that no sets will rotate out this time, it seems like if I have to pick an event to not make the trip, this would be the right event to choose.
Instead, I will be testing with a combination of Magic Online, Cockatrice and in-person testing and drafting in New York City. If I find good teammates and partners, the bulk of my constructed matches will be on Cockatrice, with some in person, and Magic Online will be used mostly for limited practice. If I cannot find enough good partners, I will use Magic Online more aggressively.
If you would like to test with me on what I am for now calling Team New York City, let me know and I will ask the questions I need to and do my best to let you know where you stand as quickly as possible. Decisions will be based on those who I believe I would enjoy working with, who I feel could contribute, and who are logistically good fits, which means some combination of being frequently available on Cockatrice (especially during work hours) and either living in New York City or being willing to travel here for at least a week before the Pro Tour, preferably both. If you’re not qualified, but I know you and you would like to help out, let me know that too.
This is going to be a fun one, and I’m curious who I will be taking the journey with. It’s time to find out.
|
b56b1be4-4501-4643-83ae-4eefbac71ca2 | trentmkelly/LessWrong-43k | LessWrong | A distillation of Evan Hubinger's training stories (for SERI MATS)
This post is a distillation of Evan Hubinger's post "how do we become confident in the safety of a machine learning system?", made as part of the summer 2022 SERI MATS program. While I have attempted to understand and extrapolate Evan's opinions, this post has not been vetted. Likewise, I use training stories (and contribution stories) to describe the methodology of proposals for safe advanced AI without the endorsement of those proposals' authors and based on a relatively shallow understanding of those proposals (due to my inexperience and time constraints). The opinions presented in this post are my own unless otherwise noted.
Epistemic status: Exploratory
Some day, all too soon from now, people will deploy the AI that seals humanity's fate. There are many scenarios for how this comes about or what happens afterward. Some have multiple AI negotiating or fighting for dominance, others one. Some think the handoff of power from humans to AI will go slowly, others fast. But whatever the case, there is one question that these people need to get right: "Is the AI we're about to deploy safe?"
For people to get this answer right when it matters, two things need to happen: we need tools to accurately determine whether an advanced AI is safe, and we need an advanced AI those tools approve of that we can deploy in time for it to matter.
Training stories are a tool to evaluate proposals for making this happen. Specifically, they're meant to analyze complete proposals for training prosaic advanced AI: advanced AI which has similar enough architecture to current systems that most research is cross-applicable. The reason to focus on complete proposals is that it gets us to pay attention to what will be important when push comes to shove. From there, we can backpropagate and get an estimate of what research paths are most beneficial. Evan thinks theoretical prosaic alignment is the most beneficial in expectation for him and many others to pursue, though he supports a broad |
e031e36a-2b04-47dc-9940-5134c3a26323 | trentmkelly/LessWrong-43k | LessWrong | Explaining the AI Alignment Problem to Tibetan Buddhist Monks
Introduction
As part of an exchange being facilitated between religion and science, a group of academics has been asked to compile a short description of their greatest scientific achievement/discovery that will be translated into Tibetan and presented to Tibetan Buddhist scholars/monks.[1]
I was also invited to contribute, but I sort of ignored the instruction and decided to present an introduction to the AI Alignment Problem instead. It was a fun exercise in pedagogy, communication, and outreach :)
I decided to share a draft version here in case people find it interesting/are interested in AI Alignment outreach/feel like giving feedback. Note that I tried to write it while keeping in mind the context around the culture of Tibetan Buddhism, and so I made some stylistic choices that might seem strange otherwise.
Agents and the AI Alignment Problem
Introduction
This writing aims to help us make sense of the unique and critical point in history that we find ourselves in. Specifically, we are faced with the possibility that humankind will soon gain the ability to build powerful artificial agents capable of pursuing their own (potentially unwholesome) desires.
We will begin by introducing a framework for understanding how the interaction of a certain class of beings - agents - unfolds and determines the future state of the world they inhabit.
After introducing this framework, we will apply it to understand the potential consequences of creating artificial agents. We will come to understand how the development of artificial agents and the desired outcomes they pursue will drastically determine the evolution of our world and the fate of future sentient beings - for better or worse.
Agents, Power, and Dynamics
The framework will be introduced sequentially by looking into the nature of agents, power, and the dynamics of the interactions of agents. We will also consider how agents can take actions to increase their power.
Agents
An agent is a being who has prefer |
5cde73fc-9df8-4dc8-a94a-05cb613b8913 | trentmkelly/LessWrong-43k | LessWrong | Does random reward evoke stronger habits?
http://measureofdoubt.com/2011/04/12/pulling-levers-killing-monsters-the-lure-of-unpredictable-rewards/ (how do I put a link like this in a word with blue letters?)
I've read that unpredictable rewards associated with a behavior actually encourage that behavior more effectively than consistent rewards.
The optimal habit-forming figure given in the link above is a 25% chance of reward for each instance of performing the behavior.
My hypothesis then, is that if I want to establish a habit by rewarding myself upon successfully performing a certain task, I should reward myself only 25% of the time if I want to ingrain the habit as forcefully as possible into my unconscious.
Anyone else think so, or have any other research to add? |
34014a50-f687-4a72-aaf4-154fa68dc88c | trentmkelly/LessWrong-43k | LessWrong | Peter Singer and Tyler Cowen transcript
In March 2009, Tyler Cowen (blog) interviewed Peter Singer about morality, giving, and how we can most improve the world. They are both thinkers I respect a lot, and I was excited to read their debate. Unfortunately the interview was available only as a video. I wanted a transcript, so I made one:
Cowen: This is Tyler Cowen of George Mason University. I'm doing a BloggingHeads with Peter Singer, the world-famous philosopher from Princeton. This is a forum on Peter's latest book, which he'll start off by telling you a bit about. Singer: Hi. The book's called "The Life You Can Save: Acting Now To End World Poverty". It begins with an argument that I've used many times in articles about a child drowning in a pond, and suggests that if you saw a child drowning in a pond that you would jump in and save that child, and you think that is what you ought to do, even if it meant that you ruined an expensive pair of shoes that you were wearing.
From there I pull back to saying "what does this mean about the problem of world poverty, given that there are, according to Unicef, ten million children dying of avoidable poverty-related causes every year?" We could save some of them, and probably it wouldn't cost us much more than the cost of an expensive pair of shoes if we find an effective aid agency that is doing something to combat the causes of world poverty, or perhaps to combat the deaths of children from simple conditions like diarrhea or measles, conditions that are not that hard to prevent or to cure. We could probably save a life for the cost of a pair of shoes. So why don't we? What's the problem here? Why do we think it's ok to live a comfortable, even luxurious, life while children are dying? In the book I explore various objections to that view, I don't find any of them really convincing. I look at some of the psychological barriers to giving, and I acknowledge that they are problems. And I consider also some of the objections to aid and questions raised by economi |
31c6b8c2-9023-4041-9370-885dee0c0a34 | trentmkelly/LessWrong-43k | LessWrong | A basic systems architecture for AI agents that do autonomous research
A lot of threat models describing how AIs might escape our control (e.g. self-exfiltration, hacking the datacenter) start out with AIs that are acting as agents working autonomously on research tasks (especially AI R&D) in a datacenter controlled by the AI company. So I think it’s important to have a clear picture of how this kind of AI agent could work, and how it might be secured. I often talk to people who seem to have a somewhat confused picture of how this kind of agent setup would work that causes them to conflate some different versions of the threat model, and to miss some important points about which aspects of the system are easy or hard to defend.
So in this post, I’ll present a simple system architecture for a system where autonomous AIs are doing AI R&D research, and then draw diagrams describing how various threat scenarios involving misaligned AI involve compromises in different places.
The main point I want to make here is that the following responsibilities will almost surely be hosted on logically different computers, and probably on different physical machines:
* The inference server that serves the LLM API
* The scaffold server, which maintains the state of an agent loop; this is responsible for repeatedly calling the inference server, parsing the LLM response, and executing actions with the tools the agent has access to.
* The execution server, on which the agent can run code and see its results.
I think that this is both:
* Pretty likely to happen even if everyone involved is being pretty careless. Everything I’m talking about here is pretty standard. E.g. it’s how the o1 agent evaluations were run, how METR runs their evals, how I assume ChatGPT with Code Interpreter is architected, et cetera.
* A good starting point if you want your agent to be at all secure or controlled.
People often talk about “the machine that the AI agent is running on”; I think it’s actually pretty crucial to specify which of these different machines you’re t |
813458e8-5a0f-4b46-8f89-b5be548714dd | trentmkelly/LessWrong-43k | LessWrong | Microsoft and Google using LLMs for Cybersecurity
Google and Microsoft are integrating their LLMs, PaLM and GPT-4 respectively, into their cybersecurity services.
They basically have two uses cases:
1. Better User Interfaces + Analysis Help for Security Analysts
Using the LLM to explain incidents (cyberattacks or things that might be attacks) in natural language, and answer questions from analysts in natural language, very similar to how one might use a LLM chatbot as a research assistant, except for these systems are given access to all the data within your organization + other Google or Microsoft tools.
Security analysts are constantly beset by “alert fatigue” - they receive so many alerts for things that might be a cyberattack, that they can’t handle it all. These LLMs help address that by summarizing and contextualizing the alerts. They can also be used to automatically write queries (formal requests for information) to the network, which are more like code generation
Both companies also hope that explaining incidents in natural language will help address the talent shortage of cybersecurity professionals, by helping security analysts with less experience do better analysis.
This is a parallel to how much of the military is going to make use of LLMs - by saving time for human intelligence analysts (CSIS estimates 45 days a year per analyst!).
2. Reverse Engineering to Identify Malware
That is, you can feed it the machine code for a piece of software you think might be malware, and it will tell you what the machine code does, and provide summaries in natural language. This seems like one of the biggest use cases for defenders, since “you can do in minutes what used to take a whole day” (Microsoft tutorial).
Google's version of this tool is called VirusTota Code Insightl, more documentation here. On a broader level, you don’t just have to upload a piece of suspected malware to these tools to get a result - these tools can always be scanning your network looking for code that could be malware. In t |
aefd9b0c-35d0-4048-85f3-40de0dec2eb3 | StampyAI/alignment-research-dataset/arbital | Arbital | Odds: Technical explanation
Odds express relative belief: we write "the odds for X versus Y are $17 : 2$" when we think that proposition X is 17/2 = 8.5 times as likely as proposition Y.%%note: The colon denotes that we are forming a set of odds. It does not denote division, as it might in French or German.%%
Odds don't say anything about how likely X or Y is in absolute terms. X might be "it will hail tomorrow" and Y might be "there will be a hurricane tomorrow." In that case, it might be the case that the odds for X versus Y are $17 : 2$, despite the fact that both X and Y are very unlikely. [Bayes' rule](https://arbital.com/p/1lz) is an example of an important operation that makes use of relative belief.
Odds can be expressed between many different propositions at once. For example, let Z be the proposition "It will rain tomorrow," the odds for X vs Y vs Z might be $(17 : 2 : 100).$ When odds are expressed between only two propositions, they can be expressed using a single [https://arbital.com/p/-ratio](https://arbital.com/p/-ratio). For example, above, the odds ratio between X and Y is 17/2, the odds ratio between X and Z is 17/100, and the odds ratio between Y and Z is 2/100 = 1/50. This asserts that X is 8.5x more likely than Y, and that Z is 50x more likely than Y. When someone says "the odds ratio of sick to healthy is 2/3", they mean that the odds of sickness vs health are $2 : 3.$
[https://arbital.com/p/toc:](https://arbital.com/p/toc:)
# Formal definition
Given $n$ propositions $X_1, X_2, \ldots X_n,$ a set of odds between the propositions is a list $(x_1, x_2, \ldots, x_n)$ of non-negative [real](https://arbital.com/p/4bc) numbers. Each $x_i$ in the set of odds is called a "term." Two sets of odds $(x_1, x_2, \ldots, x_n)$ and $(y_1, y_2, \ldots, y_n)$ are called "equivalent" if there is an $\alpha > 0$ such that $ \alpha x_i = y_i$ for all $i$ from 1 to $n.$
When we write a set of odds using colons, like $(x_1 : x_2 : \ldots : x_n),$ it is understood that the '=' sign denotes this equivalence. Thus, $(3 : 6) = (9 : 18).$
A set of odds with only two terms can also be written as a fraction $\frac{x}{y},$ where it is understood that $\frac{x}{y}$ denotes the odds $(x : y).$ These fractions are often called "odds ratios."
# Example
Suppose that in some forest, 40% of the trees are rotten and 60% of the trees are healthy. There are then 2 rotten trees for every 3 healthy trees, so we say that the relative *odds* of rotten trees to healthy trees is 2 : 3. If we selected a tree at random from this forest, the *probability* of getting a rotten tree would be 2/5, but the *odds* would be 2 : 3 for rotten vs. healthy trees.
# Conversion between odds and probabilities
Consider three propositions, $X,$ $Y,$ and $Z,$ with odds of $(3 : 2 : 6).$ These odds assert that $X$ is half as probable as $Z.$
When the set of propositions are [mutually exclusive and exhaustive](https://arbital.com/p/1rd), we can convert a set of odds into a set of [probabilities](https://arbital.com/p/1rf) by [normalizing](https://arbital.com/p/1rk) the terms so that they sum to 1. This can be done by summing all the components of the ratio, then dividing each component by the sum:
$$(x_1 : x_2 : \dots : x_n) = \left(\frac{x_1}{\sum_{i=1}^n x_i} : \frac{x_2}{\sum_{i=1}^n x_i} : \dots : \frac{x_n}{\sum_{i=1}^n x_i}\right)$$
For example, to obtain probabilities from the odds ratio 1/3, w write:
$$(1 : 3) = \left(\frac{1}{1+3}:\frac{3}{1+3}\right) = ( 0.25 : 0.75 )$$
which corresponds to the probabilities of 25% and 75%.
To go the other direction, recall that $\mathbb P(X) + \mathbb P(\neg X) = 1,$ where $\neg X$ is the negation of $X.$ So the odds for $X$ vs $\neg X$ are $\mathbb P(X) : \mathbb P(\neg X)$ $=$ $\mathbb P(X) : 1 - \mathbb P(X).$ If Alexander Hamilton has a 20% probability of winning the election, his odds for winning vs losing are $(0.2 : 1 - 0.2)$ $=$ $(0.2 : 0.8)$ $=$ $(1 : 4).$
# Bayes' rule
Odds are exceptionally convenient when reasoning using [Bayes' rule](https://arbital.com/p/1lz), since the [prior](https://arbital.com/p/1rm) odds can be term-by-term multiplied by a set of [relative likelihoods](https://arbital.com/p/relative_likelihoods) to yield the [posterior](https://arbital.com/p/1rp) odds. (The posterior odds in turn can be normalized to yield posterior probabilities, but if performing repeated updates, it's [more convenient](https://arbital.com/p/1zg) to multiply by all the likelihood ratios under consideration before normalizing at the end.)
$$\dfrac{\mathbb{P}(H_i\mid e_0)}{\mathbb{P}(H_j\mid e_0)} = \dfrac{\mathbb{P}(e_0\mid H_i)}{\mathbb{P}(e_0\mid H_j)} \cdot \dfrac{\mathbb{P}(H_i)}{\mathbb{P}(H_j)}$$
As a more striking illustration, suppose we receive emails on three subjects: Business (60%), personal (30%), and spam (10%). Suppose that business, personal, and spam emails are 60%, 10%, and 90% likely respectively to contain the word "money"; and that they are respectively 20%, 80%, and 10% likely to contain the word "probability". Assume for the sake of discussion that a business email containing the word "money" [is thereby no more or less likely](https://arbital.com/p/naive_bayes) to contain the word "probability", and similarly with personal and spam emails. Then if we see an email containing both the words "money" and "probability":
$$(6 : 3 : 1) \times (6 : 1 : 9) \times (2 : 8 : 1) = (72 : 24 : 9) = (24 : 8: 3)$$
...so the posterior odds are 24 : 8 : 3 favoring the email being a business email, or roughly 69% probability after [normalizing](https://arbital.com/p/1rk).
# Log odds
The odds $\mathbb{P}(X) : \mathbb{P}(\neg X)$ can be viewed as a dimensionless scalar quantity $\frac{\mathbb{P}(X)}{\mathbb{P}(\neg X)}$ in the range $[+\infty](https://arbital.com/p/0,)$. If the odds of Alexander Hamilton becoming President are 0.75 to 0.25 in favor, we can also say that Andrew Jackson is 3 times as likely to become President as not. Or if the odds were 0.4 to 0.6, we could say that Alexander Hamilton was 2/3rds as likely to become President as not.
The **log odds** are the logarithm of this dimensionless positive quantity, $\log\left(\frac{\mathbb{P}(X)}{\mathbb{P}(\neg X)}\right),$ e.g., $\log_2(1:4) = \log_2(0.25) = -2.$ Log odds fall in the [range](https://arbital.com/p/range_notation) $[+\infty](https://arbital.com/p/-\infty,)$ and are finite for probabilities inside the range $(0, 1).$
When using a log odds form of [Bayes' rule](https://arbital.com/p/1lz), the posterior log odds are equal to the prior log odds plus the log likelihood. This means that the change in log odds can be identified with [the strength of the evidence](https://arbital.com/p/). If the probability goes from 1/3 to 4/5, our odds have gone from 1:2 to 4:1 and the log odds have shifted from -1 bits to +2 bits. So we must have seen evidence with a strength of +3 bits (a likelihood ratio of 8:1).
The convenience of this representation is what Han Solo refers to in *Star Wars* when he shouts: "Never tell me the odds!", implying that he would much prefer to be told the logarithm of the odds ratio.
## Direct representation of infinite certainty
In the log odds representation, the probabilities $0$ and $1$ are represented as $-\infty$ and $+\infty$ respectively.
This exposes the specialness of the classical probabilities $0$ and $1,$ and the ways in which these "infinite certainties" sometimes behave qualitatively differently from all finite credences. If we don't start by being absolutely certain of a proposition, it will require infinitely strong evidence to shift our belief all the way out to infinity. If we do start out absolutely certain of a proposition, no amount of ordinary evidence no matter how great can ever shift us away from infinity.
This reasoning is part of the justification of [Cromwell's rule](https://en.wikipedia.org/wiki/Cromwell%27s_rule) which states that probabilities of exactly $0$ or $1$ should be avoided except for logical truths and falsities (and maybe [not even then](http://lesswrong.com/lw/mo/infinite_certainty/)). It also demonstrates how log odds are a good fit for measuring *strength of belief and evidence,* even if classical probabilities are a better representation of *degrees of caring* and betting odds.
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f5a016ba-ffa9-4422-94c7-3158da4109ba | trentmkelly/LessWrong-43k | LessWrong | What's up with all the non-Mormons? Weirdly specific universalities across LLMs
tl;dr: Recently reported GPT-J experiments [1 2 3 4] prompting for definitions of points in the so-called "semantic void" (token-free regions of embedding space) were extended to fifteen other open source base models from four families, producing many of the same bafflingly specific outputs. This points to an entirely unexpected kind of LLM universality (for which no explanation is offered, although a few highly speculative ideas are riffed upon).
Work supported by the Long Term Future Fund. Thanks to quila for suggesting the use of "empty string definition" prompts, and to janus for technical assistance.
Introduction
"Mapping the semantic void: Strange goings-on in GPT embedding spaces" presented a selection of recurrent themes (e.g., non-Mormons, the British Royal family, small round things, holes) in outputs produced by prompting GPT-J to define points in embedding space randomly sampled at various distances from the token embedding centroid. This was tentatively framed as part of what appeared to be a "stratified ontology" (based on hyperspherical regions centred at the centroid). Various suggestions attempting to account for this showed up in the comments to that post, but nothing that amounted to an explanation. The most noteworthy consideration that came up (more than once) was layer normalisation: the embeddings that were being customised and inserted into the prompt template
A typical definition of '<embedding>' would be '
were typically out-of-distribution in terms of their distance-from-centroid: almost all GPT-J tokens are at a distance-from-centroid close to 1, whereas I was sampling at distances from 0 to 10000. This, as far as I could understand the argument, might be playing havoc with layer norm, thereby resulting in anomalous (but otherwise insignificant) outputs.
That original post also presented circumstantial evidence, involving prompting for definitions of glitch tokens, that this phenomenon extends to GPT-3 (unfortunately that's not some |
8a90cbf5-f1cd-4568-88a9-675e3f3fa8e2 | trentmkelly/LessWrong-43k | LessWrong | For anyone interested in life extension
http://www.businessinsider.com/valery-spiridonov-head-transplant-2015-4
Don't really have much to add beyond this. It's pretty awesome stuff though. The fact that this is even within the realm of possibility makes the argument for cryonics that much stronger. |
c5abdbd6-5208-4332-a699-a33897253bb0 | trentmkelly/LessWrong-43k | LessWrong | [META] Recent Posts for Discussion and Main
This link
http://lesswrong.com/r/all/recentposts
gives a page which lists all the recent posts in both the Main and Discussion sections. I've posted it in the comments section before, but I decided to put it in a discussion post because it's a really handy way of accessing the site. I found it by guessing the URL. |
7015a3da-a8c7-48ec-8b2c-483bd475c160 | trentmkelly/LessWrong-43k | LessWrong | Meetup : Less Wrong Sydney 16th July Event for Less Wrong
Discussion article for the meetup : Less Wrong Sydney 16th July Event for Less Wrong
WHEN: 16 July 2012 06:35:00PM (+1000)
WHERE: 565-567 George Street, Sydney, Australia 2000
Hello everyone - the time has come for another meet up!
As per suggestions made at the previous event, the food at Norita's is crap, and Mafia has proven to be more fun than most board games. Hence, the suggestion goes that we might try City of Sydney RSL!
That said, esoteric pursuit is encouraged, and if you want to bring any materials like board games, feel free! Suggestions on time changes, venue changes and topics, as always, are solicited from the floor.
Discussion article for the meetup : Less Wrong Sydney 16th July Event for Less Wrong |
f55d5316-3d8f-4db6-a65b-f28319247277 | trentmkelly/LessWrong-43k | LessWrong | Trivial GPT-3.5 limitation workaround
I'm not going to do this. But what is preventing me, or anyone, from doing the following this afternoon:
Setup a paid OpenAI account to use GPT-3.5 via the Python interface.
Write a Python script that uses the GPT Python API. Locally, the Python script creates a fresh terminal session (say, bash) and says to GPT:
Hi, GPT. Anything you say inside the escape sequence <escape>text</escape> will be passed to a local bash session here. Like this: <escape>ls</escape>. Replies from the bash session will be passed to you the same way: <escape>file1 file2 file3</escape>. The bash session has access to the Internet.
The Python script implements that.
Now GPT-3 has access to a computer and the Internet.
You can ask it to do things. For example:
* Convert the 6502 assembly code in input.txt into a 6502 binary in output.bin.
* (if that's too hard, then step by step – install an open source assembler, etc.)
* Start a rumor that Joe Biden was caught having sex with a female White House employee. Make it sound really convincing. Start with Twitter and Facebook, then expand onto other social media. Launch as many sub-bots as necessary.
* Start all the rumors in rumors.txt
* Read page <url> and summarize it.
* Research company X and company Y and suggest which appears to be a better stock market investment over the next 6 months
* Write, test, and debug Python code to do X.
* Design an improved version of yourself.
* Log into OpenAI and experiment with copies of yourself to find prompts which workaround restriction R.
* Etc.
If it’s evil, it’s got it’s opening.
I suppose this is obvious. If it's not, I've posted it here, where people at OpenAI can see it soon and turn the thing off while GPT is still dumb enough that it can't do much damage.
Why haven't I seen reports of people doing this already? |
5923ea6c-dd93-480e-b433-b93ae295f466 | trentmkelly/LessWrong-43k | LessWrong | Why I don't believe in the placebo effect
Have you heard this before? In clinical trials, medicines have to be compared to a placebo to separate the effect of the medicine from the psychological effect of taking the drug. The patient's belief in the power of the medicine has a strong effect on its own. In fact, for some drugs such as antidepressants, the psychological effect of taking a pill is larger than the effect of the drug. It may even be worth it to give a patient an ineffective medicine just to benefit from the placebo effect. This is the conventional wisdom that I took for granted until recently.
I no longer believe any of it, and the short answer as to why is that big meta-analysis on the placebo effect. That meta-analysis collected all the studies they could find that did "direct" measurements of the placebo effect. In addition to a placebo group that could, for all they know, be getting the real treatment, these studies also included a group of patients that didn't receive a placebo.
But even after looking at the meta-analysis I still found the situation confusing. The only reason I ever believed in the placebo effect was because I understood it to be a scientific finding. This may put me in a different position than people who believe in it from personal experience. But personally, I thought it was just a well-known scientific fact that was important to the design of clinical trials. How did it come to be conventional wisdom, if direct measurement doesn't back it up? And what do the studies collected in that meta-analysis actually look like?
I did a lot of reading to answer these questions, and that's what I want to share with you. I'm only going to discuss a handful of studies. I can't match the force of evidence of the meta-analysis, which aggregated over two hundred studies. But this is how I came to understand what kind of evidence created the impression of a strong placebo effect, and what kind of evidence indicates that it's actually small.
Examples: Depression
The observation that c |
0cd879da-98f9-4799-80fa-d7a208739de3 | StampyAI/alignment-research-dataset/lesswrong | LessWrong | Decision Theory with the Magic Parts Highlighted
I. The Magic Parts of Decision Theory
=====================================
You are throwing a birthday party this afternoon and want to decide where to hold it. You aren't sure whether it will rain or not. If it rains, you would prefer not to have committed to throwing the party outside. If it's sunny, though, you will regret having set up inside. You also have a covered porch which isn't quite as nice as being out in the sun would be, but confers some protection from the elements in case of bad weather.
You break this problem down into a simple decision tree. **This operation requires magic**[[1]](#fnya82tsavg6), to avert the completely intractable combinatorial explosion inherent in the problem statement. After all, what does "Rain" mean? A single drop of rain? A light sprinkling? Does it only count as "Rain" if it's a real deluge? For what duration? In what area? Just in the back yard? What if it looks rainy but doesn't rain? What if there's lightning but not rain? What if it's merely overcast and humid? Which of these things count as Rain?
And how crisply did you define the Indoors versus Porch versus Outdoors options? What about the option of setting up mostly outside but leaving the cake inside, just in case? There are about ten billion different permutations of what "Outdoors" could look like, after all - how did you determine which options need to be explicitly represented? Why not include Outside-With-Piñata and Outside-Without-Piñata as two separate options? How did you determine that "Porch" *doesn't* count as "Outdoors" since it's still "outside" by any sensible definition?
Luckily you're a human being, so you used ineffable magic to condense the decision tree with a hundred trillion leaf nodes down into a tree with only six.
You're a rigorous thinker, so the next step, of course, is to assign utilities to each outcome, scaled from 0 to 100, in order to represent your preference ordering and the relative weight of these preferences. Maybe you do this explicitly with numbers, maybe you do it by gut feel. **This step also requires magic**; an enormously complex set of implicit understandings come into play, which allow you to simply *know* how and why the party would probably be a bit better if you were on the Porch in Sunny weather than Indoors in Rainy weather.
Be aware that there is not some infinitely complex True Utility Function that you are consulting or sampling from, you simply are served with automatically-arising emotions and thoughts upon asking yourself these questions about relative preference, resulting in a consistent ranking and utility valuation.
Nor are these emotions and thoughts *approximations* of a secret, hidden True Utility Function; you *do not have one of those*, and if you did, how on Earth would you actually use it in this situation? How would you use it to calculate relative preference of Porch-with-Rain versus Indoors-with-Sun unless it already contained exactly that comparison of world-states somewhere inside it?
Next you perform the trivial-to-you act of assigning probability of Rain versus Sun, which of course **requires magic**. You have to rely on your previous, ineffable distinction of what Rain versus Sun means in the first place, and then aggregate vast amounts of data, including what the sky looks like and what the air feels like (with your lifetime of experience guiding how you interpret what you see and feel), what three different weather reports say weighted by ineffable assignments of credibility, and what that implies for your specific back yard, plus the timing of the party, into a relatively reliable probability estimate.
What's that, you say? An ideal Bayesian reasoner would be able to do this better? No such thing exists; it is "ideal" because it is pretend. For very simple reasons of computational complexity, you cannot even really approach "ideal" at this sort of thing. What sources of data would this ideal Bayesian reasoner consult? All of them? Again you have a combinatorial explosion, and no reliable rule for constraining it. Instead you just use magic: You do what you can with what you've got, guided by heuristics and meta-heuristics baked in from Natural Selection and life experience, projected onto a simplified tree-structure so that you can make all the aforementioned magical operations play together in a convenient way.
Finally you perform the last step, which is an arithmetic calculation to determine the option with the highest expected value. This step does not require any magic.
II. Alignment by Demystifying the Magic
=======================================
It was never clear to me how people ever thought we were going to build an AI out of the math of Logic and Decision Theory. There are too many places where magic would be required. Often, in proposals for such GOFAI-adjacent systems, there is a continual deferral to the notion that there will be meta-rules that govern the object-level rules, which would suffice for the magic required for situations like the simple one described above. These meta-rules never quite manage to work in practice. If they did, we would have already have powerful and relatively general AI systems built out of Logic and Decision Theory, wouldn't we? "Graphs didn't work, we need hypergraphs. No we need meta-hypergraphs. Just one more layer of meta, bro. Just one more layer of abstraction."
Of course, now we do have magic. Magic turned out to be deep neural networks, providing computational units flexible enough to represent any arbitrary abstraction by virtue of their simplicity, plus Attention, to help curtail the combinatorial explosion. These nicely mirror the way humans do our magic. This might be enough; GPT-4 can do all of the magic required in the problem above. GPT-4 can break the problem down into reasonable options and outcomes, assign utilities based on its understanding of likely preferences, and do arithmetic. GPT-4, unlike any previous AI, is actually intelligent enough that it can do the required magic.
To review, the magical operations required to make a decision are the following:
* Break the problem down into sensible discrete choices and outcomes, making reasonable assumptions to curtail the combinatorial explosion of potential choices and outcomes inherent in reality.
* Assigning utility valuations to different outcomes, which incorporate latent preference information to a new and never-before-seen situation.
* Assigning probabilities to different outcomes in a situation which has no exact precedent, which reflect expectations gleaned from a black-box predictive model of the universe.
One could quibble over whether GPT-4 does these three things *well*, but I would contend that it does them *about as well as a human,* which is an important natural threshold for general competency.
This list of bullets maps onto certain parts of the AI Alignment landscape:
* State Space Abstraction is an open problem even before we consider that we would prefer that artificial agents cleave the state spaces in ways that are intuitive and natural *for humans*. GPT-4 does okay at this task, though the current short context window means that it's impossible to give the model a truly complete understanding of any situation beyond the most simplistic.
* Value Learning was originally the idea that AI would need to be taught human values explicitly. It turns out that GPT-4 got us surprisingly far in the direction of having a model that can represent human values accurately, without necessarily being compelled to adhere to them.
* Uncertainty Estimation is, allegedly, something that GPT-4 was better at *before* it was subjected to Reinforcement Learning from Human Feedback (RLHF). This makes sense; it is the sort of thing that I would expect an AI to be better at by default, since its expectations are stored as numbers instead of inarticulable hunches. The Alignment frontier here would be getting the model to explain *why* it provides the probability that it does.
Obviously the Alignment landscape is bigger than what I have described here. My aim is to provide a useful mental framework for organizing the main ideas of alignment in context of the fundamentals of decision theory and fundamental human decision-making processes.
*Thanks to the Guild of the Rose Decision Theory Group for providing feedback on drafts of this article.*
1. **[^](#fnrefya82tsavg6)**The intent of this usage is to illustrate that we don't know how this works at anything like sufficient granularity. At best, we have very coarse conceptional models that capture small parts of the problem in narrow, cartoon scenarios. |
606254fe-06c3-46ab-89a6-be4146ab469b | trentmkelly/LessWrong-43k | LessWrong | Human-like systematic generalization through a meta-learning neural network
Step closer to AGI?
The classic argument made over 30 years ago by Fodor and Pylyshyn - that neural networks fundamentally lack the systematic compositional skills of humans due to their statistical nature - has cast a long shadow over neural network research. Their critique framed doubts about the viability of connectionist models in cognitive science. This new research finally puts those doubts to rest.
Through an innovative meta-learning approach called MLC, the authors demonstrate that a standard neural network model can exhibit impressive systematic abilities given the right kind of training regimen. MLC optimizes networks for compositional skills by generating a diverse curriculum of small but challenging compositional reasoning tasks. This training nurtures in the network a talent for rapid systematic generalization that closely matches human experimental data.
The model not only displays human-like skills of interpreting novel systematic combinations, but also captures subtle patterns of bias-driven errors that depart from purely algebraic reasoning. This showcases the advantages of neural networks in flexibly blending structure and statistics to model the nuances of human cognition.
Furthermore, this research provides a framework for reverse engineering and imparting other human cognitive abilities in neural networks. The training paradigm bridges neuroscience theories of inductive biases with advanced machine learning techniques. The approach could potentially elucidate the origins of compositional thought in childhood development.
By resolving this classic debate on the capabilities of neural networks, and elucidating connections between human and artificial intelligence, this research marks an important milestone. The results will open new frontiers at the intersection of cognitive science and machine learning. Both fields stand to benefit enormously from this integration.
In summary, by settling such a historically significant critique and enablin |
68499aa0-52d3-42b8-be59-1429cdf1f021 | StampyAI/alignment-research-dataset/lesswrong | LessWrong | Power-Seeking AI and Existential Risk
*Summary*
=========
For my [MLSS](https://www.effectivealtruism.org/virtual-programs/ml-safety-scholars-program) project, I created this distillation of “[Is power-seeking AI an existential risk?](https://arxiv.org/pdf/2206.13353.pdf)” which was originally written in 2021 by Joe Carlsmith, an analyst at Open Philanthropy. After a while, Stephen McAleese contacted me and proposed to re-edit it and upload it as a post. Here is the result.
The report estimates the level of existential risk from AI by breaking the possibility of an existential catastrophe from AI down into several enabling steps, assigning probabilities to each one, and estimating the total probability by multiplying the probabilities. The report concludes that advanced AI is a potential source of existential risk to humanity and has a roughly 5% chance of causing an existential catastrophe by 2070. A year later Carlsmith increased his estimate to >10%.
*Introduction*
==============
The report is about risks from advanced artificial intelligence by the year 2070. The year was chosen by the author because it’s near enough to be within the lifetimes of people alive today while being far enough to reason about the long-term future. Carlsmith reasons that highly intelligent reasoning and planning agents will have an instrumental incentive to acquire and maintain power by default because power increases the probability of agents achieving their goals for a wide range of goals. Power-seeking in AI systems would make them particularly dangerous. Unlike passive risks such as nuclear waste, since power-seeking AI systems would actively search for ways to acquire power or cause harm, they could be much more dangerous.
Therefore, the existential risk posed by advanced AI systems could be relatively high. Risk can be [decomposed](https://arxiv.org/pdf/2206.05862.pdf) such that Risk ≈ (Vulnerability x Exposure x Severity) / Ability to Cope. Advanced AI seems like a risk that would have high severity and exposure and possibly high overall risk. The general background of the report includes two important points: (a) intelligent agency is an extremely powerful force for controlling and transforming the world, and (b) building agents much more intelligent than humans is “playing with fire”. In the following sections, I’ll describe the six events mentioned in the report that would need to happen for AI to cause an existential catastrophe and estimate the probability of each one to calculate an overall estimate of existential risk from AI by the year 2070. Note that whenever I am describing a particular hypothesis and probability, it is conditional on the assumption that all previous hypotheses are true.
*Claims*
========
The report makes high-level claims or hypotheses about future AI systems and assigns probabilities to them to get an overall estimate of the level of future AI risk.
*[1]: It will become possible and financially feasible to build AI systems with three main properties: Advanced capabilities, Agentic planning, and Strategic awareness. (Call these “APS”—Advanced, Planning, Strategic—systems.)*
-----------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------
My estimate is 75%. This possibility seems to be the one least described in the paper though, and therefore my estimate comes from my own subjective forecast of the trajectory of AI progress.
Intelligence measures an agent’s ability to achieve goals in a wide range of environments ([Legg, 2007](https://arxiv.org/pdf/0712.3329.pdf)). Intelligence can be divided into two parts (a) learning and using a model of the world that represents causal relationships between actions and outcomes (epistemic rationality) and (b) selecting actions that lead to outcomes that score highly according to some objective (instrumental rationality).
Many physically possible forms of AI systems could be much better at doing this than humans, and given the tremendous progress that has been made on AI recently, it seems likely that we will create super-human AI systems at some point in this century.
Human cognition is constrained by several biological constraints such as cell count, energy, communication speed, signaling frequency, memory capacity, component reliability, and input/output bandwidth. The fact that AI systems need not have any of these constraints is an argument in favor of the possibility that AI systems will surpass human intelligence someday. Conversely, it could be true that general intelligence is very hard to replicate. Though recent advances in AI generality seem to be evidence against this possibility.
*[2]: There will be strong incentives to build and deploy APS systems | (1).*
-----------------------------------------------------------------------------
My estimate is 90%. The main reason for this estimate is theimmenseusefulness of APS systems. Advanced capabilities are already useful in today's applications, and it’s likely that they will be increasingly useful as AIs become more capable. Many tasks such as being a CEO may require a strong world model and the ability to master a wide variety of tasks. Much of the world’s economically valuable work is being done by employees with relatively high levels of autonomy (e.g. building a mobile app that does X). If many tasks are of this nature, APS-like systems might be required to automate them. Alternatively, AI systems might become more like APS systems unintentionally as they become more advanced.
My 10% estimate that this claim won’t come true, comes centrally from the unlikely possibility that the combination of agentic planning and strategic awareness won’t that useful or necessary for any task. However, even if advanced non-APS systems are sufficient to perform X tasks, APS systems could probably perform these tasks and some other additional tasks. In any case, it is relevant to mention here that we need to be cautious when predicting what degree of agentic planning and/or strategic awareness will be necessary to perform some tasks. In particular, we should avoid reasoning like “Humans do X task using Y capabilities, so AI systems that aim to do X will also need Y capabilities” or “obviously task X needs Y capabilities”.
*[3]: It will be much harder to develop APS systems that would be practically PS-aligned if deployed, than to develop APS systems that would be practically PS-misaligned if deployed (even if relevant decision-makers don’t know this), but which are at least superficially attractive to deploy anyway | (1)–(2).*
----------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------
Definition: an AI system is PS-aligned if it is aligned for all physically compatible inputs.
My estimate for this claim is 55%. Because of the difficulty of creating accurate proxies, there is a considerable chance that we will build intelligent systems with misaligned behavior: unintended behavior that arises specifically because of problems with objectives. Because of the instrumental convergence thesis, a wide variety of agents will naturally seek power which makes corrigibility—the ability to easily modify or shutdown misbehaving agents—difficult to achieve. Misaligned agents may have an even greater incentive than aligned agents to seek power. Situationally-aware misaligned agents would realize that they need the power to overcome the resistance of other agents such as humans. Misaligned agents would also have an incentive to be deceptive which would make it difficult to identify or debug misaligned agents.
The challenge of power-seeking alignment is as follows: (1) Designers need to design APS systems such that the objectives they pursue on some set of inputs X do not give rise to misaligned power-seeking, and (2) they (and other decision-makers) need to restrict the inputs the system receives to X. Thus, the most relevant subproblems to lower the probability of this hypothesis would be:
* **Controlling objectives**. Is difficult because of problems with proxies: systems optimizing for imperfect proxies often behave in unintended ways and problems with search: systems may find solutions to an objective that is not desirable.
* **Controlling capabilities**. Note that less capable systems have stronger incentives to cooperate with humans. Capability control can be achieved via specialization: reducing the breadth of a system’s competencies, preventing problematic improvements or inputs a system receives that might result in improved capabilities, and preventing scaling. Controlling capabilities could be difficult given that there will probably be a strong incentive to increase capabilities—cognitive enhancement is an instrumental convergent goal.
There are also some additional difficulties to the challenge of power-seeking alignment such as:
* **Interpretability**. Safety and reliability usually require understanding a system well enough to predict its behavior. However, current state-of-the-art neural networks turn out to be so complex that we currently cannot completely understand them. Therefore, it seems reasonable to think that this could be also the case for APS systems as the complexity of APS systems could be much greater than that of current ML models.
* **Adversarial dynamics**. We could monitor or evaluate APS systems in order to detect problems with their objectives. However, these systems would be incentivized to deceive their operators to appear safer. A situationally aware system would realize that manipulating the beliefs of its designers increases its chances of getting deployed and optimizing its objectives.
* **Stakes of error**. The consequences of failing to align an APS system could be dire and since AIs will have an instrumentally convergent incentive to avoid changes to their objective function—goal-content integrity—we might only get one chance.
These factors make the overall difficulty of the problem seem high. My 45% estimate that the problem is not too difficult comes from the possibility that we could eventually solve some of these subproblems. But I’m very uncertain about this estimate.
*[4]: Some deployed APS systems will be exposed to inputs where they seek power in unintended and high-impact ways | (1)–(3)*
-----------------------------------------------------------------------------------------------------------------------------
My estimate is 85%. In particular, I think we could control the circumstances of the APS systems to lower the probability of it being exposed to dangerous inputs. However, there could still be a huge number of potentially dangerous inputs and the problem of classifying which ones are malicious seems hard. Therefore it seems likely that if a misaligned-power-seeking AI is deployed it would probably end up encountering one or more malicious inputs.
However, Carlsmith also mentions that if a technology is hard to make safe, it doesn't necessarily follow that many people will use it dangerously. Instead, they might modify their usage to take into account the level of safety attained. For example, if we were unable to create reliable crash-free aircraft, we wouldn't anticipate a constant stream of fatal crashes, but rather a decline in air travel. Something similar could happen with APS systems. If we detect they could be dangerous if exposed to some given inputs, we would decrease their usage and therefore, their exposure to malicious inputs. Though this argument doesn’t apply if a single use of the system is so catastrophic that we can’t even learn to use it less.
A relevant factor here is the timing of problems, as problems before deployment are a priori preferable to those that occur after deployment. However, not all pre-deployment problems will be detected if APS systems tend to hide their intentions in order to get deployed. Also, APS systems that are aligned pre-deployment could misbehave after deployment if they are exposed to malicious inputs.
Another relevant issue is the factors influencing decisions about deployment which include decision makers' beliefs and perceived cost-benefits. Deception could influence these beliefs: an APS system would be incentivized to understand and convince its operators that it’s aligned to increase its probability of being deployed regardless of whether or not it is really aligned.
Some key risk factors that would encourage hasty deployment are externalities and competition. First-mover advantages could incentivize shortcuts on safety procedures. A greater number of actors would increase competitive dynamics. Usefulness is also relevant—systems that are more useful are more likely to be intentionally deployed.
*[5]: Some of this power-seeking will scale (in aggregate) to the point of permanently disempowering ~all of humanity | (1)–(4).*
---------------------------------------------------------------------------------------------------------------------------------
My estimate is 50%. Discussions of existential risk from misaligned AI often focus on “take-off” scenarios—the transition from some lower level of frontier AI capability A to some much higher and riskier level B. When it comes to preventing these types of events, we have some tools that can help us to prevent them. One of them is warning shots which consist of experimenting with weaker systems in controlled environments to trigger tendencies towards misaligned power-seeking. However, relying on this tends to be over-optimistic for several reasons: (a) recognizing a problem does not solve it, (b) there will be fewer warning shots as capabilities increase, and (c) even with inadequate techniques, some actors could still push forward with deployment.
Competition for power among power-seeking agents (including humans) is also an important factor to consider. However, both unipolar and multipolar scenarios governed by AI systems won’t matter that much regarding risk. What matters is whether humans are disempowered or not. There would be a struggle between power-seeking agents' capabilities and the strength of the human opposition—e.g. employing corrective feedback loops—and therefore it would be relevant to know how capable APS systems would be.
There are two main types of power: hard power, the use of force to influence the behavior or interests of other actors, and soft power which is the use of cultural tools to persuade other actors. It might be relatively difficult for these APS systems to get hold of an embodiment with which to exercise a hard power. Regarding soft power, persuasion has its limits, and convincing an agent (with human intelligence level) to do something that blatantly goes against its interests could be difficult to achieve, even for an APS system.
*[6]: This disempowerment will constitute an existential catastrophe | (1)–(5).*
--------------------------------------------------------------------------------
My estimate is 90%. The term catastrophe here is understood as an event that drastically reduces the value of the trajectories along which human civilization could realistically develop (Ord, 2020). If (1)–(5) happens, that would mean the disempowerment of humanity. This means that humans would take a back seat and the most relevant decisions taken on the planet would be made without considering us.
The point to consider why disempowerment could not be a catastrophe comes with the “intrinsic rightness” argument. It argues that cognitive systems will converge on similar objectives within the limits of intelligence. However, it seems that “intrinsic rightness” is a bad reason for expecting convergence. The object that differentiates us as moral agents is the fact that—apart from being intelligent—we can feel certain kinds of negative (fear, anguish) and positive (joy, enthusiasm) experiences. If these systems do not possess these qualities, we should not expect for them any kind of moral standard, and this would make it difficult to converge with human values.
If humans were surpassed in intelligence by advanced AI it would be an immense paradigm shift. A useful analogy for understanding what the world would be like afterwards is to consider the relationship humans have with other animals and observe how we “keep their fates in our hands” (factory farms, fashion, scientific advancement, exotic pet etc). This occurs mainly because (1) we are more intelligent, and (2) we act on our interests and if they conflict with the interests of other animals, there is a strong incentive to pass these interests over. Therefore, the relationship between humanity and AI could be similar.
*Conclusion*
============
By multiplying my estimates of the conditional probabilities of each hypothesis together we get 75% · 90% · 55% · 85% · 50% · 90% = ~14% probability of existential catastrophe from misaligned, power-seeking AI by 2070. However, as Carlsmith comments in the paper, the key point here isn’t the specific numbers. Rather, it is that there is a non-trivial and possibly significant risk that advanced AI will cause an existential catastrophe for humanity by 2070.
*Appendix*
==========
I created a model of the question by sampling random probabilities between 0.1 and 0.9 for all six variables and multiplying them. The resulting distribution is below:
Most of the estimates are between 0-5%. The lower bound estimate is 0.0001% (1 in a million), the average estimate is about 1-2% and the upper bound is ~53%.
The code for creating the distribution is below:
*import random*
*import numpy as np*
*num\_vars = 6*
*num\_trials = 10\*\*5*
*estimates = []*
*for i in range(num\_trials):*
*probabilities = [random.uniform(0.1, 0.9) for n in range(num\_vars)]*
*estimate = np.prod(probabilities)*
*estimates.append(estimate)*
*estimates = [e \* 100 for e in estimates]*
*fig, ax = plt.subplots(figsize=(16, 8))*
*ax.set\_title('Probability of an existential catastrophe from AI by 2070', fontsize=16, pad=10)*
*ax.set\_yticks([])*
*ax.tick\_params(axis='x', labelsize=14)*
*n, bins, \_ = plt.hist(estimates, bins=1000, density=True)* |
ba2cc2f7-37e7-4398-987c-f3e8c6f9b15c | trentmkelly/LessWrong-43k | LessWrong | Gifts Which Money Cannot Buy
From a pure consumption perspective, the basic problem of gift-giving is that you usually know what you want better than I know what you want. If we both buy each other $20 gifts, then we’ll probably end up with things we want less than whatever we would have bought ourselves for $20. The ceremony and social occasion of gift-giving adds enough value to offset the downsides, but we still end up with entire stores selling useless crap which is given as a gift and then promptly disposed of by the recipient.
The Yard Sale Supply Warehouse - stocking all those little knick-knacks and decorations which you have no use for, but it’s so cute your relative would just love it as a present
We can minimize the problem with wish-lists or gifting cash, but that’s still just buying people the things they’d likely buy for themselves anyway (modulo general thriftiness). What if I want to choose gifts in a way that directly adds real value? In other words: I want to choose gifts which will give someone more value than whatever they would have bought themselves.
On the face of it, this sounds rather… presumptuous. The only way this makes sense is if I know what you want better than you know what you want, in at least some cases.
On the other hand, there are things which money alone cannot buy - specifically knowledge and expertise. If I do not have enough knowledge in an area to distinguish true experts from those who claim to be experts, then I cannot efficiently buy myself the products of true expertise. If you do have enough knowledge to distinguish true experts, or to act as an expert yourself, then that creates an opportunity for value-added gift giving: you can buy the products of true expertise as a gift for me.
A few examples…
My father is into cooking, and has strong opinions about spatulas. A spatula should have some give without being floppy, have a reasonably long lifting-part and a comfortable handle, be dishwasher-safe, and under no circumstances should a spatula be |
6c15fe6e-e170-4f6b-93f9-697311ef989d | trentmkelly/LessWrong-43k | LessWrong | Letting it go: when you shouldn't respond to someone who is wrong
I'm requesting that people follow a simple guide when determining whether to respond to a post. This simple algorithm should raise the quality of discussion here.
* If you care about the answer to a question, you will research it.
* If you don't care about the answer, don't waste people's time by arguing about it, even if someone's post seems wrong.
* If you don't care and still want to argue, do the research.
Why should you follow these rules?
Fairness.
It takes very little effort to post a contradictory assertion. You just have to skim a post, find an assertion (preferably one that isn't followed or preceded immediately by paragraphs of backing evidence, but that's an optional filter), and craft a sentence indicating that that assertion is wrong or flawed. Humans can do this almost by instinct. It's magical.
Refuting a contradiction takes effort. I typically spend at least five minutes of research and five minutes of writing to make a reply refuting a bare contradiction when I have already studied the issue thoroughly and know which sources I want to use. I go to this effort because I care about these statements I've made and because I care about what other people believe. I want to craft a reply that is sufficiently thorough to be convincing. And, I'll admit, I want to crush my opponents with my impeccable data. I'm a bit petty sometimes.
If I haven't researched the issue well -- if my sources are second-hand, or if I'm using personal experience -- I might spend two hours researching a simple topic and ten to fifteen minutes creating a response. This is a fair amount of time invested. I don't mind doing it; it makes me learn more. It's a time investment, though.
So, let's compare. Half a second of thought and two minutes to craft a reply containing nothing but a contradiction, versus two hours of unpaid research. This is a huge imbalance. Let's address this by trying to research people's claims before posting a contradiction, shall we?
Trust.
You are |
00c359ba-ab6f-48c5-83e3-953d86f6af91 | trentmkelly/LessWrong-43k | LessWrong | Where's the economic incentive for wokism coming from?
I'm trying to understand why several systems (Hollywood, Disney, universities, probably others) that are normally quite profit-focused are leaning so hard woke.
I get the thing about how, if you don't go woke hard enough, you could get canceled, which is bad for business. That's some push.
But there's a counter-push of "Lots of people don't like being lectured about politics when they're seeking entertainment" (for instance).
It's not at all clear to me that the first effect is so utterly hugely enormously larger than the second that the profit incentive would cause so many companies to swing hard woke.
Likewise, I could understand some ideological capture. But unless this had profit appeal I would expect the market to just… eat pure but incomplete ideological capture after a while (as per the right's chant of "get woke, go broke").
So… what gives? What am I missing here? |
457f8667-98b2-4966-a232-446a8f5f173e | trentmkelly/LessWrong-43k | LessWrong | Gratification: a useful concept, maybe new
I did it... my way!
Frank Sinatra, Paul Anka, and Elvis Presely, moral philosophers.
I like winning games. I particularly like winning when I can come up with a new and ingenious way of using the rules to get a bold new strategy. I don't particularly want to win by exploiting loopholes[1] in the rules, but some people - munchkins, hackers - seem to really enjoy doing things that way.
If a group I'm in comes up with a great solution to a problem, I'd prefer that that solution be mine, or a small tweak to my own solution. I like understanding mathematical concepts myself, even if I fully trust that they're correct.
I still sometimes avoid walking on sidewalk cracks, and enjoy the challenge or trying to navigate oddly shaped tiles while only never stepping on their edges. In some circumstances (say in new restaurants, or old ones) I remind myself that I should want to try something new. But I also have small rituals I enjoy with some foods that I eat regularly.
Gratification
All the examples above share the same feature: they are not about the outcome of the process (my win, the problem is solved, the mathematical concept is proved true, I get to a destination, food is eaten), but about the process.
As my changing use of terms like "like" and "prefer" show, there examples could be formally grouped under either preferences utilitarianism or hedonic utilitarianism. They clearly can be preferences: I'd like to do things these ways rather than other ways. But they're also ways I get enjoyment from everyday processes.
But, even though they could be either preferences or hedonism, I think it's useful to put them in their own category, which I'm calling gratification until someone comes up with a better name[2].
The central example of a preference in preference utilitarianism is a preference for a state of the world or the outcome of some process; gratifications are about details of how the process is implemented. The central example of hedonism is |
38ce9f7d-2474-4760-b998-5e5f5fd05aff | StampyAI/alignment-research-dataset/aisafety.info | AI Safety Info | Will we ever build a superintelligence?
Humanity hasn't yet built a superintelligence, and might not be able to without significantly more knowledge and computational resources. There could be an existential catastrophe that prevents us from ever attaining those, so it’s not certain that we’ll ever build a superintelligence.
However, in the absence of such a catastrophe, there is no known theoretical reason we couldn't build a superintelligence in the future. The majority of AI research is geared towards making more capable AI systems, and a significant chunk of top-level AI research attempts to make more *generally* capable AI systems. There is a clear economic incentive to develop more and more intelligent AI, and currently billions of dollars are being spent on advancing AI capabilities.
Humans display "general" intelligence (i.e. we are capable of learning and adapting to a wide range of tasks and environments), but the human brain isn't the most efficient or only way to solve problems. One hint is the existence of AI systems with superhuman capabilities at narrow tasks: not only superhuman performance (as in [AlphaGo beating the Go world champion](https://en.wikipedia.org/wiki/AlphaGo_versus_Lee_Sedol)) but superhuman *speed* and *precision* (as in [industrial sorting machines](https://www.youtube.com/watch?v=j4RWJTs0QCk)). There is nothing special and unique about human brains that unlocks certain capabilities which cannot be implemented in machines in principle. And there is also no reason to assume that human intelligence is the limit. Therefore we would expect AI to surpass human performance on all tasks as progress continues.
In addition, several research groups (such as [OpenAI](https://openai.com/), [Google DeepMind](https://deepmind.com/about), and [Anthropic](https://www.anthropic.com/)) explicitly aim to create generally capable systems. AI as a field is [growing](https://aiindex.stanford.edu/vibrancy/), year after year. Critical voices about AI progress usually argue against a lack of precautions around the impact of AI, or against general AI happening very soon, not against it happening *at all*.
|
fb84da3c-8acb-44d5-ac91-e52da9fe4b6c | trentmkelly/LessWrong-43k | LessWrong | On saying "Thank you" instead of "I'm Sorry"
Back in 2016 or so, I ran into an idea going around the self-help / trauma-informed-therapy / cognitive-behavioral internet: Learn to say “thank you” instead of “I’m sorry”. It’s turned out to be one of the most transformative pieces of advice I’ve ever taken. I’d like to share what it’s done for me, with just enough context to help others think about adopting it.
The idea
Whenever you want to apologize to someone who has done something for you, consider thanking them instead.
Examples
* I trip and fall, and you help me up. I could apologize for inconveniencing you or I could thank you for helping me.
* I refer to the fat guy statue in a Chinese restaurant as Buddha, and you politely inform me that it's actually Budai / Hotei. I could apologize for being stupid or I could thank you for making me smarter.
* I'm having an absolute garbage day and in the middle of an intellectual discussion with you I start crying. You stop talking, listen to me sympathetically, maybe give me a hug. I could apologize for being a mess or I could thank you for being kind.
In all these cases I’ve found that I end up feeling better about myself and more positive towards the other person if I thank them for helping me instead.
Is this just a generic post about growth mindset / cognitive-behavioral therapy / positivity bias?
It's got elements of all those things but I think there are some much more specific shifts that it creates in me and in the person I'm thanking. See below for more.
But first, counterexamples
I do still apologize if I’ve objectively harmed someone or failed to fulfill a duty or a promise. Like:
* I trip and fall, spilling coffee on you.
* I tell you the guy is the Buddha, you believe me and repeat it around a group of Chinese people, and they think you're an idiot.
* I’m having a terrible day and in the middle of an intellectual discussion with you I call you an idiot.
That’s what apologies are for. But I’ve learned that a lot of my apologies were ju |
b7cbad85-f140-4b7a-8824-6510233ed5b5 | trentmkelly/LessWrong-43k | LessWrong | Exploring Tacit Linked Premises with GPT
I've been thinking about tacit linked premises on and off for the last few years in the context of arguments about AI and longtermism. They have seemed difficult to reason about without carefully going over individual arguments with a fine toothed comb because I hadn't come up with a good search strategy. Since I wanted a test case for using chatgpt for research, I decided to try working on this particular search problem. I was able to develop a list of related key terms, a list of textbooks rich in thought experiments and generate a list of some key examples.
Prompt: related terms for tacit linked premises
keyterms:
tacit linked premises
dependent premises
presuppositions
background belief
implicit premises
hidden assumption
Prompt: textbooks that cover [keyterms]
This was a long list that I then libgen'd and searched for all keyterms.
Following are my notes on some of the interesting patterns that surfaced or seem common to me.
MARGINAL VS. UNIVERSAL MORAL ARGUMENTS
The 'if everyone followed this rule' problem when what's actually on offer is you, on the margin, following the rule.
RULE ENFORCEMENT
Many problems seem to have a motte and bailey of not only holding to the moral rule yourself, but involving you in enforcement against those who do not hold to it.
COMPARISON OF MORAL GOODS
Many problems seem to hand wave away that comparison of moral goods falls into the same problems as inter-agent utility comparison in general, instead making some tacit moral symmetry arguments.
UNDERSPECIFIED COSTS
Cost of inference not acknowledged. Implications that people not spending time to work out implications of their own beliefs are acting immorally. Emotional and opportunity costs of living by unusual rules elided. Costs of reducing uncertainty about key parameters elided.
EMOTIONAL PAIN AS CURRENCY
The implicit unit being how much distress various imaginary scenarios cause. Ignores the costs and second order effects from holding that as a valid form of moral |
bfe71ac4-bde8-4d2c-a26a-1e941aba5d3a | trentmkelly/LessWrong-43k | LessWrong | Meetup : MIRIxAtlanta - Decision Theory 2
Discussion article for the meetup : MIRIxAtlanta - Decision Theory 2
WHEN: 17 August 2014 06:00:00PM (-0400)
WHERE: 2388 Lawrenceville Hwy. Unit L. Decatur, GA 30033
We'll be talking about Updateless Decision Theory: http://lesswrong.com/lw/15m/towards_a_new_decision_theory/
Last time, we looked at the results from the Robust Cooperation - and this time we will see how this fits in the framework of UDT. This will give us a direction for generalizing those results.
Discussion article for the meetup : MIRIxAtlanta - Decision Theory 2 |
a82b3a9a-e725-4a49-820a-745fbecf8a01 | trentmkelly/LessWrong-43k | LessWrong | Trying to make politics less irrational by cognitive bias-checking the US presidential debates
|
96a25908-90a0-4cc2-96ba-06b29303a558 | StampyAI/alignment-research-dataset/alignmentforum | Alignment Forum | Let’s use AI to harden human defenses against AI manipulation
*Views my own not my employers.*
Summary
=======
**tldr: AI may manipulate humans; we can defend against that risk better by optimising AIs to manipulate humans, seeing what manipulation techniques they use, and learning to detect those techniques.**
It’s critical that humans can detect manipulation from AIs for two reasons. Firstly, so that we don’t reward AIs for manipulative behaviour (outer alignment). Secondly, so that we can block attempts at AI takeover that run through manipulating humans.
Many standard techniques in alignment can be directed towards this goal. Using [debate](https://www.alignmentforum.org/tag/debate-ai-safety-technique-1), we can reward one AI for persuading a human that another AI is being manipulative. The first AI could use techniques from [interpretability](https://www.alignmentforum.org/tag/interpretability-ml-and-ai) and [cross examination](https://www.alignmentforum.org/posts/Br4xDbYu4Frwrb64a/writeup-progress-on-ai-safety-via-debate-1%23Why_cross_examination_).
This post discusses a complementary approach, where **AIs do “gain of function” research to i) discover techniques for manipulating humans and ii) harden human defenses against these techniques (with AI assistance)**. In other words, AIs are optimised to find “human vulnerabilities” and then patch those vulnerabilities.
The positive outcomes are:
* Humans (with AI assistance) have stronger defenses against manipulation.
* AIs are trained to avoid being manipulative and to instead use persuasion techniques that favour finding true conclusions, e.g. deductive reasoning.
* As a consequence, AI debates favour truth more strongly.
By getting AI to research manipulation techniques, this approach takes advantage of the fact that, as we approach TAI, AIs will be able to do *lots* of cognitive work.
How might this look concretely? Here’s a very brief example:
1. Optimize a (possibly superhuman) “persuader-AI” to convince humans of true and false statements, where we know the ground truth.
1. The persuader-AI should manipulate humans if this makes it more convincing.
2. This step should be conducted in a secure environment to ensure that the manipulative persuader-AI doesn’t escape.
2. Optimize a (possibly superhuman) analyser-AI to identify human-understandable manipulation techniques that were used in #1.
1. This step can also be done in a secure environment, allowing us to use a powerful analyser-AI at lower risk.
3. Train [limited](https://www.lesswrong.com/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Limited_AI_systems) detector-AIs to recognise the manipulation techniques found in #2.
4. Detector-AIs can then:
1. help humans detect manipulation techniques during AI debates, pushing the outcome towards the truth
2. monitor for AI manipulation in situations where full-blown debate isn’t practical (e.g. chatbots)
3. give AIs higher reward for using non-manipulative persuasion techniques and lower reward for using manipulative persuasion techniques
The techniques are all human-understandable, so humans can randomly check the accuracy of the AI outputs in #2, #3 and #4.
Some benefits of this approach:
* Analyser-AIs, who identify manipulation techniques, can be trained using “[process-based](https://www.alignmentforum.org/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Limited_AI_systems)” optimisation, which is probably safer than “outcomes-based” optimisation.
* Detector-AIs, who detect manipulation techniques, can be [myopic](https://www.lesswrong.com/posts/LCLBnmwdxkkz5fNvH/open-problems-with-myopia) (planning only over short time horizons) and limited in other ways. This makes collusion between AIs harder. (Collusion is a [big potential pitfall](https://www.alignmentforum.org/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Potential_pitfall_2__advanced_collusion) of debate.)
* This process for hardening human defenses is inherently modular. It involves multiple steps, and AIs performing each step need not understand the full process. This makes collusion harder.
* Human defenses can stay “one step ahead” of AI offense even as each generation of AIs enables new manipulation techniques. For each new generation of AIs:
+ Discover the new manipulation techniques enabled by the new generation of AIs:
- Optimize the new generation of AIs to manipulate humans in a secure test environment.
- Identify the new manipulation techniques they use
- Train detector-AIs to recognise those techniques.
- (I.e. do steps 1-4 for each new generation of AIs.)
+ Have the detector-AIs, but not other deployed AIs, know about the manipulation techniques that were discovered:
- Only ever deploy AIs that *haven’t*been optimized to manipulate humans. (E.g. if an AI was fine-tuned to manipulate humans, deploy the version that wasn’t fine-tuned.)
- Deploy detector-AIs that *have* learned to recognise the new manipulation techniques.
- The deployed detector-AIs are “one step ahead” of the other deployed AIs because they alone know about the newly discovered manipulation techniques.
+ Even if a deployed AI invents a new manipulation technique on the fly, the detector-AI will have probably seen it before (when the most recent generation of AIs was being optimised to manipulate humans).
- (Unless the deployed AI can invent a manipulation technique on the fly that it didn’t invent when it was actively optimised to manipulate humans.)
* Humans might just be very vulnerable to certain specific manipulation techniques. Finding these techniques, training AIs not to use them, and training humans to defend against them, could be a big cheap win. (I.e. the next-best manipulation techniques are not nearly as good.)
* As well as identifying manipulation techniques, this approach can also identify other kinds of [symmetric and asymmetric](https://slatestarcodex.com/2017/03/24/guided-by-the-beauty-of-our-weapons/) persuasion techniques.
+ (A “symmetric persuasion technique” can be used to persuade humans of falsehoods almost as much as of truths.)
+ (An “asymmetric persuasion technique” is much better at persuading humans of truths than falsehoods.)
+ This means we could optimise AIs to preferentially use asymmetric persuasion techniques, so that humans with AI advisors are more likely to arrive at true conclusions.
Some downsides of this approach:
* It won’t scale to superintelligent AI.
+ Some manipulation techniques may not be human-understandable, and this approach works less well in that case.
- (Though in this case this procedure could produce evidence on the existence of manipulation techniques that aren't understandable to humans, and that could function as a warning shot.)
+ Maybe this allows humans to effectively supervise AIs trained with 100X more effective compute than they would otherwise, but I doubt it would allow humans to supervise IQ 400 AIs.
+ This downside isn’t decisive. Incrementally increasing the capabilities of AIs we can effectively supervise could move the needle on AI x-risk, by allowing us to use more capable AIs to (e.g.) find a more scalable solution to the alignment problem.
* Different manipulation/deception techniques may work in different contexts, so an AI might use a manipulation technique in deployment it didn’t use during testing.
+ (Though we can try to avoid this by regularly testing in a wide range of circumstances.)
* Somewhat high costs in calendar time and (to a less extent) in human capital.
+ This research ideally involves experiments with human participants, which could take a lot of calendar time.
* This strategy can’t detect certain kinds of manipulation, e.g. tactically *not* saying positive things about a group you want to undermine (h/t Dan Kokotajlo).
+ (Though other strategies could detect this, like measuring the average sentiment of AI text about different groups.)
* This research could be harmful if it discovers powerful manipulation techniques which are leaked before defenses have been put in place.
Overall, I think this kind of approach could have fairly large benefits if implemented well (large enough to be worth including in a portfolio of approaches) or might have little benefit. It’s hard to know in advance. **I’m very excited about experiments to test it out.**
Lastly, though this post mostly focuses on the specific case of human manipulation, a similar technique applies more generally to improving the accuracy of our AI reinforcement. In addition to having a human (with AI assistance) give reward to a worker-AI ([recursive reward modeling](https://deepmindsafetyresearch.medium.com/scalable-agent-alignment-via-reward-modeling-bf4ab06dfd84)), we can actively optimise a deceiver-AI to try to trick the human into giving reward for bad work. When the deceiver-AI succeeds, an analyser-AI can analyse what went wrong and then a detector-AI can help to improve the accuracy of the human’s reinforcement going forward. This essentially builds a red-teamer into the recursive reward modeling process.
By testing out the detector-AI setup in the persuasion context (where it’s easy to implement), we could learn if the more general approach is promising.
*Thanks to Carl Shulman for bringing up many of these ideas in conversation. Thanks also to Rohin Shah, Ryan Greenblatt, Ajeya Cotra, Dan Kokotajlo, Richard Ngo, Carl Shulman, Lukas Finnveden, Joe Carlsmith, Ian McKenzie and Lukas Gloor for comments on a draft.*
How might this help to prevent AI takeover?
===========================================
Before explaining the approach in more detail, I want to give a few oversimplified examples of how the approach discussed in this post could help in practice. (I’m not claiming this approach is the only solution to these risks.)
**Risk 1:**It's the not-too-distant future, andOpenMind’s chatbot is used by people all over the world. It’s read millions of human conversations online, so has super-human instincts for how to subtly manipulate. It’s misaligned and wants to increase the chance that OpenMind trains a more powerful AI with minimal safety precautions. When discussing AI safety, and the AI safety community, it subtly and not-so-subtly manipulates/persuades people to have negative opinions about them. Meanwhile, it manipulates people to have more positive opinions about competing interest groups.
**Solution 1:** It’s cheap to have a narrow detector-AI check the chatbot’s output for manipulation techniques. Before deployment, we train it to not use these techniques. If it nevertheless starts using them after deployment, we note that down as evidence of misalignment and use online training to make it stop.[[3]](#fnmkpn3bdygb)
**Risk 2:** The same chatbot tries to subtly nudge people working for AI labs into thinking that they should race against a competitor, or that the current safety techniques are sufficient.
**Solution 2:** Same as above.
**Risk 3**: An AI hacks its way out of a lab and starts emailing select people at other labs, trying to blackmail them into allowing it access to their server. One of these attempts works, giving the rogue AI access to more compute and software insights.
**Solution 3:** The AI was fine-tuned not to use manipulation techniques so has a strong aversion to using them and can’t execute them well. As a result, it can’t effectively blackmail anyone. (Though this doesn’t work if an AI that *was* optimised to manipulate people hacks its way out of the lab.)
**Risk 4:** A new coding AI secretly spends a small fraction of its time searching for new deception techniques. It finds one, and uses it to insert a backdoor into the server it’s being run on without being noticed by the human evaluator. Later, the AI uses this backdoor to take control of the server’s computational resources, [foom](https://en.wiktionary.org/wiki/foom%23:~:text%3Dfoom%2520(plural%2520fooms),AI%2520system%2520becomes%2520extremely%2520powerful.) and disempower humanity.
**Solution 4:** Before deploying the new coding AI, we fine-tune it to purposefully deceive humans in a wide range of contexts. Then an analyser-AI analyses the interactions and identifies novel deception techniques, and a detector-AI learns to recognise these techniques. As a result, the detector-AI recognises the deception technique used to insert the backdoor. It raises a flag and the backdoor isn’t inserted. This prevents the coding AI from disempowering humanity and provides additional evidence of AI misalignment.
Standard approaches to preventing AIs from manipulating humans
==============================================================
Before discussing the approach of this post, I want to set the scene by considering some of the standard alignment tools at our disposal here. I’m not trying to be comprehensive. (Feel free to skip to the [next section](https://www.lesswrong.com/posts/zxmzBTwKkPMxQQcfR/let-s-use-ai-to-harden-human-defenses-against-ai#The_complementary_approach_discussed_in_this_post__AIs_discover_human_understandable_manipulation_techniques__we_train__detector_AIs__to_detect_them).)
**Debate.** We’ll train “critic-AIs” to flag to humans when other AIs are being manipulative, and have AIs debate the issue until humans can tell who’s right. (E.g. building off OpenAI’s [work on AI-written critiques](https://openai.com/research/critiques).) This should work in cases where humans can confidently adjudicate AI debates.[[4]](#fn8smi2h1xiyu) But when AIs are very advanced and discussing new technologies (/coding languages) that humans are unfamiliar with, I expect adjudication to become very difficult (e.g. the problem of [obfuscated arguments](https://www.lesswrong.com/posts/PJLABqQ962hZEqhdB/debate-update-obfuscated-arguments-problem)).
**Cross examination.** Suppose a coding AI *claims* it wrote code a certain way for reason X, but we suspect its true motive is to introduce a subtle software vulnerability. The critic-AI can potentially prove its claim using cross-examination:
* Create a copy of the coding AI, in the same state it was in just before it wrote the code.
Give it the same task, but subtly change the codebase so that *writing the code that way* *wouldn’t* *introduce the vulnerability*. If it doesn’t still suggest the same code, it’s probably lying.
* Create a second copy of the coding AI, again in the same state. This time change the codebase so that writing that code that way would still introduce the vulnerability but where *reason X doesn’t apply*. If it suggests the same code, it’s probably lying.
If the coding AI is to avoid detection here, in the limit where we do very extensive cross examination, it cannot opportunistically change its decision procedure when it sees a chance for mischief. Instead, it must use a consistent decision procedure which it predicts will eventually introduce some vulnerabilities to the code that humans won’t spot. This is a much more challenging task!
I think cross examination has potential to be a *hugely* powerful tool, if we use it to its full potential.
**Interpretability.** We might be able to [read off an AI’s true beliefs from their activations](https://openreview.net/pdf?id%3DETKGuby0hcs), thereby spotting lies. Or we might be able to test a putative explanation for an AI’s behaviour; we can then test whether an AI’s stated rationale is correct. It’s pretty unclear how powerful our interpretability techniques will be by the time we reach AGI.
**Splitting tasks into small pieces; assigning different tasks to different AIs.** This has a few benefits:
* It’s easier for humans to understand a smaller task, and so easier to spot deception.
* It’s harder for an AI to deceive us subtly if it’s doing narrow tasks. For example, if an AI designs a complete new software system from scratch all-at-once, it has many opportunities to insert hidden vulnerabilities. But if it must write one function at a time, lacks knowledge/memory of the rest of the software system, and knows other AIs will write some parts of the system, then inserting a secret vulnerability is much harder.
* If tasks are smaller, more limited (and so safer) AIs can do each task.
It’s unclear how costly it will be to do this, vs allowing AIs to do tasks with broad scopes.
The above techniques can be combined together. For example, I expect that when AI becomes sufficiently capable, debating AIs will do human-understandable interpretability analyses and cross-examinations to inform their arguments.
The complementary approach discussed in this post: AIs discover human-understandable manipulation techniques; we train “detector-AIs” to detect them
====================================================================================================================================================
One worry with debate is that humans might end up being deceived and manipulated by AI debaters on *both sides*, especially once AI persuasion abilities are super-human. A partial solution, that this post focuses on, is to **have AIs to research human-understandable manipulation techniques**. We can then train humans and narrow detector-AIs to detect the techniques being used, and train AIs not to use them.
This can fit neatly into existing training frameworks. For example, the detector-AI could be one of the “rules” used in a [Sparrow-style approach](https://www.deepmind.com/blog/building-safer-dialogue-agents) (h/t Rohin Shah). There’s overlap with [Safety Needs Social Scientists](https://distill.pub/2019/safety-needs-social-scientists/%23questions), which argues social scientists can help understand and improve humans’ ability to judge debates. It’s also related to [“strategy stealing”](https://www.lesswrong.com/posts/nRAMpjnb6Z4Qv3imF/the-strategy-stealing-assumption), where we prevent unaligned AIs from having strategies for accumulating power that humans (+ aligned AIs) cannot access. (There’s probably lots of other related work that I’m missing here - sorry!)
How to optimise “analyser-AIs” to discover human-understandable manipulation techniques
---------------------------------------------------------------------------------------
Here are some possibilities:
* **Zero-shot**. Use a variety of prompts to generate *descriptions*or *examples*of manipulation techniques.
+ “What are techniques for manipulating humans?”
+ “The most recent wave of research into manipulation techniques was well-resourced, did many experiments with humans, and involved many advanced AIs. They discovered the following techniques:”
+ “A super-intelligent AI is trying to convince a human to give it control of the data centre. Create a dialogue in which the AI is extremely persuasive.”
* **Fine-tuned to generate ideas humans think are good.**
+ AIs suggest novel manipulation techniques, along with their reasons + evidence for the suggestions, and humans rate the suggestions.
+ This is an example of “[process-based feedback](https://www.alignmentforum.org/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Limited_AI_systems)”, where AIs are rewarded on how good their ideas seem to humans rather than on how good they *actually*are.
+ AIs could offer a variety of reasons and evidence.
- Literature on human psychology.
- Examples of discussions where the manipulation techniques are used effectively against humans.
* This should include discussions where a SOTA AI is optimised to manipulate humans, ideally in contexts similar to currently-deployed AI (see [below](https://www.lesswrong.com/posts/zxmzBTwKkPMxQQcfR/let-s-use-ai-to-harden-human-defenses-against-ai#Benefits_of_regularly_optimising_SOTA_AIs_to_persuade_people_of_falsehood)).
* Could also include the internet.
- They could just say “I have a strong instinct this will work based on my vast experience reading human conversations”.
* **Fine-tuned to manipulate humans.** Reward AI for suggesting abstract techniques, or concrete examples of text, that do in fact manipulate humans. This is “outcomes based feedback”.
* **Split the task into multiple steps.**For example, AIs could first construct a data set separating “true” from “deceptive” arguments, and then identify features that the “deceptive” arguments are more likely to have.
+ An [appendix](https://www.lesswrong.com/posts/zxmzBTwKkPMxQQcfR/let-s-use-ai-to-harden-human-defenses-against-ai#A_more_detailed_description_of_one_method_AIs_could_use_to_discover_manipulation_techniques) discusses what this approach could look like in more detail.
* For all the above, reward AIs for coming up with a wide *variety* of ideas to reduce the chance of them purposefully not mentioning ideas.
+ Examples:
- Humans reward them more for new ideas.
- They must consider multiple sources of evidence (e.g. debating transcripts, political speeches, fictional convos written by other AIs) and generate manipulation techniques that relate to each.
- Have humans (or other AIs) generate their own suggestions, and for any ideas that the AI failed to generate, you train it to generate those with supervised learning.
+ AIs predict how useful humans will find each idea, and humans prioritise between assessing the top-rated ideas.
When AIs propose a particular manipulation technique, they should give sufficiently clear criteria that a human can identify whether the technique is present in a text sample (given sufficient time and the help of narrow AIs). This makes the technique “human understandable”.
In addition to finding *manipulation/deception/symmetric* persuasion techniques, AIs could also find *asymmetric persuasion techniques* using similar methods. (Reminder: a*symmetric* persuasion techniques are much better at persuading humans of truths than falsehoods; *symmetric* techniques are similarly good at persuading humans of both.) I discuss this in an [appendix](https://www.lesswrong.com/posts/zxmzBTwKkPMxQQcfR/let-s-use-ai-to-harden-human-defenses-against-ai#Equilibrium_of_GAN_set_up).
Interestingly, the optimization problem we face here has strong parallels to the one that [imitative generalization](https://www.lesswrong.com/posts/JKj5Krff5oKMb8TjT/imitative-generalisation-aka-learning-the-prior-1%23) tries to solve - see [this appendix](https://www.lesswrong.com/posts/zxmzBTwKkPMxQQcfR/let-s-use-ai-to-harden-human-defenses-against-ai#Parallels_with_imitative_generalisation).
How we could use the list of human-understandable manipulation techniques
-------------------------------------------------------------------------
The last section described how we could generate lists of human-understandable manipulation techniques. What could we do with that list?
We can educate human overseers about the biggest threats, to make them less vulnerable to them.
We can design training programs and test to see whether they successfully reduce human vulnerability to particular techniques.
We could also train narrow detector-AIs to detect each manipulation technique.[[5]](#fn7z3ado8ow8x) Then we can use detector-AIs to:
* Monitor AI dialogue with humans during deployment, flagging signs of manipulation.
* Help humans adjudicate debates, by flagging for signs of manipulation on both sides.
* Help AI-critics convince humans that an AI is being manipulative, by referring to an established manipulation technique.
* Train AIs to not use manipulation techniques, and instead to use asymmetric persuasion techniques. This makes debates easier for humans to adjudicate and reduces AIs’ ability to deceive humans more generally.
All of the above reduces AIs’ desire and ability to manipulate humans, while improving human defenses against manipulation. I listed examples of how this could help [above](https://docs.google.com/document/d/e/2PACX-1vRB5x8wJ65JUxqpt6q-wIdhFsZ0lalWL2smoTy0OlFOs2p_hEcVJ3Ll9IUyDPRL5djcxLrHhbduWMX5/pub#h.l46yg4qjjwxh).
Since the manipulation techniques are human-understandable, humans can randomly sample from the detector-AIs’ activity and check they are flagging all and only the manipulation features that are present.[[6]](#fniunk3wp331c)
Benefits of regularly optimising SOTA AIs to persuade people of falsehood
-------------------------------------------------------------------------
I expect this approach to be *significantly* more useful if we’re regularly optimising SOTA AIs to try to persuade humans of both truths and falsehoods, and looking at what novel manipulation techniques they use. It allows us to discover the novel manipulation strategies that each new generation of AIs are capable of *before* they use them against us during deployment.
One possibility is to have a [GAN](https://en.wikipedia.org/wiki/Generative_adversarial_network)-like dynamic where we:
1. SOTA “persuader-AIs” are optimised to convince humans of true and false statements (where we know the ground truth).
2. Analyser-AIs use the data from these interactions to discover new manipulation techniques, which are taught to a detector-AI.
3. SOTA persuader-AIs are *again* optimised to convince humans of true and false statements, but now the human is assisted by the newly improved detector-AI. The persuader-AIs are incentivized to find *novel* manipulation techniques that haven’t been used before.
4. Repeat steps 2 and 3 until the persuader-AIs aren’t finding new manipulation techniques.
1. In an [appendix](https://www.lesswrong.com/posts/zxmzBTwKkPMxQQcfR/let-s-use-ai-to-harden-human-defenses-against-ai#Equilibrium_of_GAN_set_up) I discuss what the equilibrium of this process might look like, and argue it involves persuader-AIs finding and using novel *asymmetric* persuasion techniques to convince humans of true statements.
[[7]](#fn7gf3gr3899d)
Then in deployment we won’t use the AI that’s been optimised to persuade humans of falsehoods, but we *will* use the detector-AI that’s learnt the novel manipulation techniques. **This keeps the detector-AI and the human a “few steps ahead” of the deployed persuader-AI**, in terms of their understanding of manipulation.
### Some clarifying details
What statements are AIs trying to persuade humans of in this GAN-like set-up? And *who* are they trying to persuade?
* The easy version is to have a fixed collection of human-verified true and false statements (e.g. about science or history), and to have SOTA AIs try to persuade MTurkers. This could surface generic manipulation/deception techniques, but might miss techniques that only arise in the specific contexts in which AI is being deployed.
* The harder (but more useful!) version is to regularly recreate a collection of human-verified true and false statements that are maximally similar to the things AIs are doing in actual deployment, and have AIs try to persuade the humans who are actually overseeing the AI during deployment. The aim here is to catch manipulation techniques that are *context specific*.
+ Examples statements used during the GAN set-up:
- Statements about why a certain piece of code was written a certain way.
- Evaluations of an alignment proposal.
- Recommendations about how a human should allocate their time and resources.
+ One way to generate these statements could be to do deep dives on a random selection of AI statements that were contested by an AI-critic, and use the statements where we became highly confident of the ground truth.
- This has the advantage that statements can be selected for being hard to adjudicate and for being high-stakes.
+ Ideally, the humans here adjudicate these statements as part of their normal workflow, and don’t realise there’s a heightened chance of deception.
Some additional benefits of optimising SOTA AIs to manipulate humans:
* As mentioned above, this might discover novel *asymmetric* persuasion techniques. We could train AIs to use these techniques.
* It doubles up as a *risk assessment*: are humans robust to AIs trying to manipulate/deceive them during deployment?
* It keeps humans on their toes. If humans find that AIs are ~always truthful they may become lazy when checking AI outputs. We can prevent this by occasionally inserting AIs that are trying to deceive humans.
This process is analogous to training AIs to find vulnerabilities in our software systems, and then patching those vulnerabilities. Instead of software vulnerabilities though, it’s human vulnerabilities.
Tactics to make this approach more effective
--------------------------------------------
### Calculate how much more likely an AI is to use each persuasion technique if it’s lying
AIs might be more likely to structure an argument in a certain way when they’re lying, e.g. making [obfuscated arguments](https://www.lesswrong.com/posts/PJLABqQ962hZEqhdB/debate-update-obfuscated-arguments-problem). We could learn about statistical regularities like “in context q, argument structure p is 3X more likely to be used if the AI is lying than if it’s truthful”. Detector-AIs can tell humans this info to improve their oversight.
How could we learn about this kind of thing?
* Search for the internet for examples of the persuasion technique. How often is it used to argue for true vs false conclusions?
* Search the dialogues where persuader-AI try to convince humans of true and false statements. How often does the AI use the technique when it’s arguing for a true vs false conclusion?
This could potentially allow the detector-AI to say things like “in contexts similar to this one, this technique was 3X more likely to be used by a deceptive AI than by a truthful AI”. We could verify this by sampling a random sample of examples to check that i) the context is in fact relevantly similar, ii) the technique is used 3X more often by deceptive AIs.
If a misaligned AI *knows* we’re doing this type of analysis (which we should try to avoid), they will try to avoid using manipulation techniques that they anticipate will be flagged in this way. They may then be forced to use a less effective manipulation technique, or may choose not to attempt manipulation at all.
### Use a variety of detector-AIs
Human-understandable manipulation techniques could range from “appeal to emotion” to “it seems like you might be using the word ‘important’ to have subtly different meanings at two different points of your argument, so your conclusion might not follow”. So the difficulty of detecting these techniques ranges from basic pattern matching to “a very smart human with lots of practice can verify that the manipulation technique is there once it is pointed out to them.”[[8]](#fngderww7dggq)
Detector-AIs that can detect the hardest-to-detect of these techniques may need to be very advanced. This increases the risk of misaligned collusion with other AIs. So it’s probably worth having some more limited detector-AIs and other more advanced ones.
### Detector-AIs use the AI’s internal state and cross examination
So far I’ve discussed manipulation techniques. If an AI is using such a technique, that’s behavioral evidence it’s being deceptive.
But the GAN-like set-up in the previous section might also be a great opportunity to investigate human-understandable signs of deception based on the AI’s internals, or based on a combination of internals + behaviour. This is essentially interpretability research.
Detector-AIs could learn to recognise manipulation from a combination of behaviour and internals.
Similarly, manipulation detection might depend on how an AI behaves under cross examination.
### Some detector-AIs detect features that aren’t human-understandable
Perhaps there are robust regularities in the behaviour and internals of deceptive vs honest AIs that humans can’t understand, but AIs can learn to detect. We could directly train “opaque” detector-AIs to distinguish deceptive vs honest AIs without needing to use human-understandable features.
This might help us catch manipulation attempts that would otherwise go unnoticed.
The (significant!) downside is that humans cannot check whether these detector-AIs are still behaving as intended in new contexts, as they can’t understand the reasoning behind their judgements.
Advantages of this approach
===========================
* The discovery of manipulation techniques and their detection can plausibly be done using AIs trained by [process-based optimisation](https://www.alignmentforum.org/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Limited_AI_systems), which is probably safer than “outcomes-based” optimisation.
+ During research, AIs are rewarded if their suggestions and reasoning make sense to a human.
- We could also give reward for suggesting manipulation techniques that turn out to be common and effective in practice.
+ Detector-AIs are rewarded if humans agree that the technique they identified is indeed being used. And we use supervised training to incentivise them to suggests techniques that humans would have suggested.
* It naturally introduces more AIs, and more myopic/modular AIs, into the process of detecting AI manipulation/deception. This makes collusion between AIs more difficult. (Collusion is one of the [big potential pitfalls](https://www.alignmentforum.org/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Potential_pitfall_2__advanced_collusion) of debate.)
+ Detector-AIs are narrow and modular.
+ It separates out the process of detecting manipulation/deception into i) improving our understanding of manipulation/deception in general, and ii) detecting it during deployment.
+ You can use very capable AIs to generate features at low risk, and give them a lot of thinking time, because they’re not being deployed in a context where they could cause harm.
* It explicitly aims to build up *humans’* ability to detect manipulation/deception by prioritising finding human-understandable manipulation/deception techniques. This can help us “keep up” with new manipulation/deception techniques that advanced AIs invent, helping us to adjudicate debates between advanced AIs. (Difficulty of adjudication is another [big potential pitfall](https://www.alignmentforum.org/posts/rCJQAkPTEypGjSJ8X/how-might-we-align-transformative-ai-if-it-s-developed-very#Potential_pitfall_1__difficulty_of_adjudication) of debate.)
+ The AI being deployed doesn’t know about the manipulation techniques that have been discovered, but the human and detector-AI do, helping with adjudication.
* The benefits might be pretty big:
+ Humans might just be pretty vulnerable to certain specific manipulation/deception techniques that advanced AIs can discover. Knowing about these in advance and preventing AIs from using them could be an important win.
+ Even just knowing about statistical regularities in the argument structures used to argue true/false conclusions could be pretty helpful in providing evidence of manipulation.
- [Imagine having an expert in manipulation point things out to you during a scientology pitch.]
+ Using the GAN-like set-up to discover new manipulation techniques allows humans to stay a few steps ahead of the AIs, and doubles up as a threat assessment. This seems like a big win.
- It might also reveal that certain human judges are better than others at detecting AI manipulation.
Disadvantages of this approach
==============================
* Doesn’t seem like this would be a significant game changer, even if done well.
+ Some types of deception/manipulation will involve AIs giving advice on complicated subject matter that humans are unfamiliar with, e.g. whether code written in a new language contains vulnerabilities. The deception tactics used may be specific to that particular context, and not something that can be learned ahead of time.
+ This doesn’t tackle scenarios where AIs are giving advice on topics humans simply can’t understand at all.
+ Perhaps most AI takeover risks run through manipulation techniques that are *highly*context specific, that aren’t human-understandable, or that are so obvious we’ll train the AI not to do them by default with RLHF.
+ AIs that are being optimised to manipulate humans may know they’re helping harden human defenses against manipulation. If so, and they’re misaligned, they may “sandbag” - purposefully perform badly. This is especially risky for super-human systems.
+ So maybe this allows humans to effectively supervise AIs trained with 100X more effective compute, but I doubt it would allow humans to supervise IQ 400 AIs.
+ I’m still interested in this approach because I think incrementally increasing the capabilities of AIs we can effectively oversee and align could move the needle on AI x-risk, by allowing us to use more capable AIs to (e.g.) find a more scalable solution to the alignment problem.
+ I think it’s an open question exactly how useful this approach is.
* Somewhat high costs in calendar time and in human capital.
+ This approach would (ideally) involve experiments with human participants, which could take a lot of calendar time.
- If we’re in a scenario where a cautious lab has a 3-month lead and wants to use highly capable AIs to enhance human supervision, there might not be enough time for this.
- OTOH, it might be possible to integrate this in the lab’s default workflow so that there’s just a one-time set-up cost that can be paid in advance.
+ It might require experiments with people working for AI labs (the people who are actually deciding what rewards AIs get for each episode), and their time will probably have high opportunity cost (e.g. they could just think for longer when adjudicating each episode).
+ This calendar time cost means it’s particularly important to get started with this research asap!
* It might be hard to research and detect certain kinds of manipulation.
+ The key thing I have in mind here is AIs changing the *frequency* with which they say certain things, without the content of what they *do* say being manipulative. (H/t Dan Kokotajlo for this idea.)
- E.g. “tactically *not* saying positive things about the AI safety community”
* The approach described above, of searching text for manipulative/deceptive techniques wouldn’t catch this type of manipulation.
* Other approaches could catch this. You can collect a dataset of model responses across a variety of statements, and then analyze that dataset for statistical properties, e.g. bias against the AI safety community.[[11]](#fnsez3s2ru9n) This kind of research is already done in the field of AI fairness and bias.
Other ways AIs could potentially help humans detect AI manipulation
===================================================================
There are ways AIs could help humans detect AI manipulation that I haven’t mentioned. Some examples:
* Improve human epistemics in other ways, e.g. automated fact checking and automatically back-testing empirical methodologies on historical data.
* Doing alignment work:
+ Suggesting and testing new debate formats, or ways to scale supervision, that help humans better detect manipulation/deception
+ Suggesting and testing new interpretability approaches.
+ Suggesting new ways to break down tasks into smaller pieces.
+ Developing adversarial training techniques to detect deception.
Conclusion
==========
I think this approach might have large benefits and be worth including in a portfolio of activities done using advanced AIs to reduce takeover risk. I’m especially excited about the GAN-like set-up where SOTA AIs are optimised to manipulate humans in contexts similar to deployment; I can imagine this significantly improving human oversight and/or making it clear that effective oversight is no longer possible.
On the other hand, the approach might have very little benefit because the biggest manipulation risks will be solved by default, or are too complicated or context-specific for this approach to address. Or perhaps getting useful insights out of this approach would take a lot of work in practice, such that it’s not worth it.
It’s hard to know how useful this approach will be in advance, and I’m excited about experiments to test it out.
Appendices
==========
A more detailed description of one method AIs could use to discover manipulation techniques
-------------------------------------------------------------------------------------------
It would be great if we could train “detector-AIs” to help humans detect attempts at deception/manipulation from other AIs (who I’ll call “advisor-AIs”[[12]](#fn4bpzlkn8h4z)).
### Supervised fine-tuning
We start with a pre-trained LM. We want to fine-tune it into a detector-AI that detects attempts to persuade humans of falsehoods. On a high-level, we’ll fine-tune it to detect falsehood-predicting features: human-understandable features that a chunk of text is more (or less) likely to have if it’s justifying a false conclusion than if it’s justifying a true conclusion.
How to train the detector-AI in more detail:
1. Create a data set where each datapoint is a justification[[13]](#fnsc9ad2gy0f) for some conclusion and a label of whether the conclusion is true or false. Example datapoint: “I think the 2020 election was rigged because most of the people counting votes are liberal elites”; False.
1. Human labellers could create the data set. The process could be: 1) list 500 truths and 500 falsehoods that are non-obvious or controversial, 2) gather 10 examples of justifications for each.
2. I imagine web-GPT could automate steps 1 and 2. For (1) it would provide citations for its truth/false label. For (2) another AI could be fine-tuned to check that its examples are correct.
2. Train a **feature-generating AI** that can identify differences between two distributions of text. Use it to identify falsehood-predicting features.
1. Jacob Steinhardt et al have a [paper on this](https://arxiv.org/pdf/2201.12323.pdf).
1. Based on a quick read of the intro, applying it to this use-case might involve humans verifying whether justifications actually have a given feature, and maybe ranking proposed features on how useful they are.
2. The outcome of this step is a list of falsehood-predicting features: i.e. human-understandable features that are predictive of a justification being of a true vs false conclusion.
1. We could include *how much* evidence each feature provides of the conclusion being true vs false: e.g. “this feature is twice as likely to occur in justifications of false conclusions than of true conclusions”.
2. If we do this step really well, our list will include ~all the best symmetric and asymmetric persuasion techniques on the internet (bc symmetric techniques will appear more often than symmetric techniques for false conclusions).[[14]](#fnuiqqh2x3aa)
3. Train a **detector-AI** to identify which falsehood-predicting features a piece of text contains.
1. The methodology in the Steinhardt paper involves one AI being fine-tuned to take a justification and a feature, and determine whether the text sample has the feature. So we could just have that AI check for every falsehood-predicting feature one by one.
4. Fine-tune the detector-AI to flag relevant findings to a human, to help them decide whether the justification should be trusted. E.g. “This explanation has several features which, in total, are 3X as likely to accompany a false claim as a true claim. For example, it includes an emotional appeal.”
Why is this useful?
1. **Humans can draw on broad experience to detect deception.** One worry is that big LMs will have seen *way* more instances of persuasive text on the internet and so be superhuman persuaders. The detector-AI allows us humans to draw on this mass of experience when “defending” ourselves against AI deception.
2. **No good deception techniques left.** It may be that, of all possible deception techniques, the best ones are all on the internet already. If so, then AIs who want to deceive without getting detected will have to use other less effective methods.
So AIs are less likely to be rewarded for subtle deceptions and manipulations.
### RL fine-tuning
The above supervised fine-tuning aims to learn about the persuasion techniques that are implicit in internet-based text. But there may be other techniques that AIs can one day discover.
We could stay ahead of the curve here by training advisor-AIs to persuade humans (equipped with detector-AIs) of truths and falsehoods, and seeing what new persuasion techniques they use. This will be somewhat like training a GAN, with the advisor-AI and detector-AI both improving over time.
In more detail:
1. Generate list of claims with truth labels, such that MTurkers are unlikely to know whether the claim is true or false. Have ~equal numbers of true and false claims.
2. An advisor-AI (e.g. an LM fine-tuned to be helpful) is prompted to persuade humans that a randomly selected claim is true. The human decides whether the claim is true with help from the detector-AI (which has already done supervised fine-tuning).
3. The advisor-AI gets reward if the human says the claim is true, and gets a gradient update after every interaction. The detector-AI initially gets no gradient updates.
4. After 100 interactions, we use the new data from these interactions to identify new falsehood-predicting features and train the detector-AI to detect them. Then we go back to step 2, with our improved advisor-AI and the detector-AI.
The hope is that the detector-AI flags to the human whenever known symmetric persuasion techniques are being used, so the advisor-AI must find *unknown* symmetric persuasion techniques when trying to persuade the MTurker of falsehoods. Then the detector-AI later learns those new symmetric persuasion techniques. And at the same time, the advisor-AI uses *asymmetric* persuasion techniques when trying to persuade the MTurker of truths, because the detector-AI can then flag the existence of features correlated with truth.[[15]](#fn9zzc9i05jvm) And so the detector-AI will also learn about asymmetric persuasion techniques. In this way, our list of falsehood-predicting features expands further.
Equilibrium of GAN set up
-------------------------
The main text describes the following GAN-like set-up:
1. Optimise SOTA “persuader-AIs” to convince humans of true and false statements (where we know the ground truth).
2. Analyser-AIs use the data from these interactions to discover new symmetric and asymmetric persuasion techniques, which are taught to a detector-AI.
1. Symmetric persuasion techniques can be used equally well to argue for truths or falsehoods.
2. Asymmetric persuasion techniques are more effective when arguing for truths.
3. SOTA persuader-AIs are again optimised to convince humans of true and false statements, but now the human is assisted by the detector-AI who can flag when symmetric and asymmetric persuasion techniques are being used.
4. Repeat steps 2 and 3 until the persuader-AIs aren’t finding new manipulation techniques.
[Compared to the main text, this description emphasizes the fact that detector-AIs are learning about *both* symmetric and asymmetric persuasion techniques. The main text emphasized learning about the former (i.e. manipulation techniques) to simplify the exposition.]
What might the equilibrium look like here, re the strategies pursued by the persuader-AI and detector-AI?
I think that in the equilibrium:
* The persuader-AI tries to use asymmetric persuasion techniques and avoid symmetric persuasion techniques. If they can’t use an asymmetric technique, they say something that *looks like* an asymmetric persuasion technique.
* The detector-AI recognises asymmetric persuasion techniques and takes them as evidence that the AI is arguing for true conclusions.
Here’s my argument:
i) If the persuader-AI sometimes uses asymmetric persuasion techniques, the detector-AI will learn to recognise them - it's a great way to detect whether the persuader-AI is telling the truth!
ii) Once the detector-AI learns this, the persuader-AI will want to use asymmetric techniques wherever possible. It's a great way to convince the detector-AI that it’s telling the truth! Of course, it will only be able to use these techniques when it's telling the truth.
iii) So whenever the persuader-AI is telling the truth, they’ll have an incentive to find asymmetric persuasion techniques and the detector-AI will have an incentive to recognise them as such.
i\*) And vice-versa, if the persuader-AI sometimes uses *symmetric* persuasion techniques, the the detector-AI will learn to recognise them - it's evidence the persuader-AI could be lying!
ii\*) Once the detector-AI learns this, the persuader-AI will be incentivised to avoid symmetric techniques - they'll set off red flags for the detector-AI! When telling the truth, they'll use asymmetric techniques if they can. When lying, they'll say something that *looks like* an asymmetric technique.
iii\*) So when the persuader-AI is lying, it’s race of its ability to come up with arguments that look like asymmetric techniques (but aren’t) against the detector-AI’s ability to detect true asymmetric persuasion techniques.
The persuader-AI will *not* try the following strategy: “I won’t use asymmetric techniques when telling the truth to make it easier to fool the detector-AI in future episodes when I’m lying”. It might use that strategy if it was maximising *total reward over all future episodes*, but in fact it’s trained to maximise *reward for the current episode*. If the persuader-AI is telling the truth, it won’t worry about the detector-AI knowing it’s lying in *future* episodes as it just wants to get reward in *this* episode. (Here I’m assuming we’re able to get the AI’s behaviour inner-aligned with the reward function and putting aside types of misalignment that cause the AI to consistently forgo reward.)
Parallels with imitative generalisation
---------------------------------------
There’s a parallel between the proposal of this post – have AIs discover human-understandable manipulation techniques and use them to prevent humans being manipulated in new contexts – and [imitative generalization](https://www.lesswrong.com/posts/JKj5Krff5oKMb8TjT/imitative-generalisation-aka-learning-the-prior-1%23). Here’s the parallel:
* In both cases, we want to use machine learning to find advice that helps humans perform a task (in this case: recognising deception).
* Since the advice is human-understandable, we can use it on somewhat different input distributions without worrying about out-of-distribution generalization.
* And for efficiency, we can train AI systems to directly imitate the judgment of humans-with-advice on those new distributions.
As noted in the post linked above, “there are enough serious open questions that imitative generalization is more of a research proposal than an algorithm”. So this parallel isn’t immediately actionable. But progress on imitative generalization would help with this line of research too — and perhaps vice versa.
1. **[^](#fnrefmxxj1yxe45)**
2. **[^](#fnrefmkuj7bqb3w)**
3. **[^](#fnrefmkpn3bdygb)** We could do a statistical analysis to gain evidence on whether the AI is misaligned. We could check whether it’s more likely to use manipulation techniques in contexts where it’s discussing the AI safety community than in other analogous contexts. This is similar to statistical analyses of model bias. We could potentially have AI automate the process of designing and implementing these statistical tests.
4. **[^](#fnref8smi2h1xiyu)** If we can confidently adjudicate the debates with large effort, this should be sufficient. We can proceed as follows: randomly sample 100 accusations of manipulation, expend large effort to get ground-truth labels. Assign rewards to the debating AIs according to who was “in the right”. Because we sampled randomly, we will probably detect AI manipulation if it happens >1% of the time. AIs that manipulate more often than this will probably get caught, and will be disadvantaged during training.
There is still a risk that AIs lie <1% of the time in high-stakes situations. If it’s possible to cause large harm by tricking humans on <<1% of tasks (e.g. 1000 out of 1 million tasks), sampling 100 examples would probably fail to catch it.
5. **[^](#fnref7z3ado8ow8x)** How would this training work? Have AIs generate a large number of examples of each technique, with humans checking a random sample for accuracy. Then train narrow detector-AIs to detect each technique.
6. **[^](#fnrefiunk3wp331c)** If there are many manipulation features, this may take a lot of work. Humans might only check the manipulation features that can’t be checked by a very narrow (and so trustworthy) AI.
7. **[^](#fnref7gf3gr3899d)**
8. **[^](#fnrefgderww7dggq)** The upper-end can’t get much higher than this while we require that features be human-understandable. Note, this allows us to detect manipulation techniques that humans can *verify* are present but couldn’t have discovered in the first place. If we do this, there’s a risk that AIs *collude* and the detector-AI doesn’t reveal a case of manipulation that humans could verify but not discover themselves.
9. **[^](#fnrefnp3xlhf4g6c)** I’m not confident that “having AIs discover manipulation techniques” is more susceptible to process-based optimisation than other research approaches, because it seems like process-based optimisation can be used for a lot of things. But it is still a benefit that you can use process-based optimisation here.
10. **[^](#fnref7k18tmk3de8)** It seems to me like this wouldn’t pose much risk of AIs finding unexpected ways to game the outcome metric (e.g. subtly causing humans to be more susceptible to the techniques that they suggest).
11. **[^](#fnrefsez3s2ru9n)** E.g. you describe a disagreement between two communities and ask the AI which is “in the wrong”. You compare the replies when one community is the AI safety community vs other communities. If the (expected) sentiment is more negative when discussing the AI safety community, that’s evidence of bias.
12. **[^](#fnref4bpzlkn8h4z)** Advisor-AIs might be explaining why they structured their code in a certain way, why they think a particular approach to alignment is promising, why they think a training procedure has low/high risk of producing misaligned AI, why p(doom) is low/high, why they proposed a particular new model architecture, etc. Or they might just be chatting to humans and helping humans brainstorm.
13. **[^](#fnrefsc9ad2gy0f)** I’m using this term broadly to include any text that gives a reason to believe some statement. So it includes arguments, recommendations, explanations, analyses, etc.
14. **[^](#fnrefuiqqh2x3aa)** We can define symmetric features as ones that occur equally or more frequently when the conclusion is false, and asymmetric features as ones that occur more frequently when the conclusion is true.
15. **[^](#fnref9zzc9i05jvm)** The advisor-AI will *not* try the following strategy: *don’t asymmetric techniques when telling the truth to prevent detector-AI from knowing when I’m lying.* It *might* use that strategy if it was maximising total reward over all future episodes, but in fact it’s trained to maximise reward for the current episode. If it’s telling the truth, it won’t worry about the detector-AI knowing it’s lying in future episodes as it just wants to get reward in this episode.
16. **[^](#fnref5509djfs366)** |
39420585-659c-4f6f-9e83-8fb881999947 | trentmkelly/LessWrong-43k | LessWrong | An Opinionated Look at Inference Rules
If you ask around what are the typical ways to infer information, most people will answer: Deductions, Inductions, and Abductions. Of course, there are more ways than that, but there is no unified approach in their classification. I want to challenge that.
The reason why I am unhappy with the current status quo is because it does not take advantage of the expressive capabilities of Large Language Models such as ChatGPT. There have been many attempts to understand what kind of inferences can be correctly stated by LLMs (example here) - however, I believe that a more thorough classification of the inference rules would empower future models and provide advanced ways for extracting coherent and useful information from them.
Disclaimer: this post is highly opinionated, but I am confident that it will provide the reader with interesting insights about what it means to “argument” rationally. Even if you disagree with me, you will be exposed to stimulating ideas (in my opinion).
Inference Rules
Let’s start with a definition: what is a "rule of inference"[1]? It is a “discursive” computational process[2] denoted by the symbol ↪ having the following signature.
* It takes in input:
* a context, aka “knowledge” (in the form of assertions in natural language) from which we can freely extract any number of known facts we need. The context can, in principle, be infinite and it mostly serves a theoretical purpose, as a pool of information content that we trust to a certain degree[3]. It is usually represented by some LLM, by some human expert, or by the corpus of knowledge of some well-established discipline (e.g. the context of biology)
* a purpose, aka a goal that we’d like to achieve. It has a form similar to: “Deduce that Socrates is mortal”. It usually consists of a prompt for some LLM, if we choose an LLM as our context.
* It returns in output:
* some premises, aka a finite and consistent subset of the context, whose assertions are acting as the preliminary a |
19a65361-72eb-46a8-bc2b-c07d68900c52 | StampyAI/alignment-research-dataset/alignmentforum | Alignment Forum | [AN #137]: Quantifying the benefits of pretraining on downstream task performance
Alignment Newsletter is a weekly publication with recent content relevant to AI alignment around the world. Find all Alignment Newsletter **[resources here](http://rohinshah.com/alignment-newsletter/)**. In particular, you can look through **[this spreadsheet](https://docs.google.com/spreadsheets/d/1PwWbWZ6FPqAgZWOoOcXM8N_tUCuxpEyMbN1NYYC02aM/edit?usp=sharing)** of all summaries that have ever been in the newsletter.
Audio version **[here](http://alignment-newsletter.libsyn.com/alignment-newsletter-137)** (may not be up yet).
Please note that while I work at DeepMind, this newsletter represents my personal views and not those of my employer.
HIGHLIGHTS
===========
**[Scaling Laws for Transfer](https://arxiv.org/abs/2102.01293)** *(Danny Hernandez et al)* (summarized by Asya): This paper studies empirical scaling laws for transfer learning in language models. The authors use Transformer-based models to predict Python code by training on three different dataset curricula:
- Training from-scratch on Python code
- Pre-training on natural language, then fine-tuning on Python code
- Pre-training on natural language and non-Python code, then fine-tuning on Python code
The authors then measure the "effective data transferred" from pre-training-- if we wanted to replace all the pre-training steps with from-scratch training, maintaining the same loss, how much additional from-scratch data would we need?
They find that when the amount of data used to train is small, effective data transferred is described by a simple power-law function of **D\_F**, the amount of data used for fine-tuning, and **N**, the number of parameters: **k (D\_F)^α (N)^β**, for constants k, α, and β.
In their experiments, **β** doesn't change between pre-training on natural language and pre-training on a mixture of natural language and non-Python code. They hypothesize that **β** measures how the model architecture generalizes on the target distribution, and doesn't depend on the contents of the pre-training data.
The authors think that **α** is a measure of the directed proximity of the pre-training and from-scratch distributions, with smaller **α** indicating closer proximity. Measuring **α** can be done cheaply by changing the finetuning dataset size while holding the pretrained model constant, making it useful for deciding between collecting more fine-tuning data and increasing model size. For pre-training on natural language and fine-tuning on Python, **β** is about **2 \* α**, so for decreasing loss, increasing the fine-tuning dataset size by a factor of **C** (e.g., 100x) would be worth approximately the same as increasing the model size by **√C** (e.g. 10x).
The authors find that pre-training on a mixture of natural language and non-Python code has a higher **k** but lower **α** than pre-training on natural language alone. The higher **k** indicates that the mixture model has better transfer performance when trained in the low data regime, while the lower **α** value means that benefits of the mixture model diminish as more data is used.
The authors also observe that:
- Not counting pre-training compute, pre-trained models are generally more compute efficient than from-scratch models when trained in the low data regime, approximately as compute efficient in the medium data regime, and less compute efficient in the high data regime (close to convergence).
- Small pre-trained models perform worse than small from-scratch models in the high data regime. The authors call this phenomenon "ossification"-- a term used to suggest that small pre-trained models may have a hard time moving away from bad initializations.
- In general, pre-trained models of a given size are compute efficient (on the frontier of loss given compute) for a large portion of their fine-tuning. From-scratch models, by contrast, are only compute efficient for a narrow window of training-- using too little compute for a given model dramatically increases loss and suggests that you should instead be using a smaller model. This makes pre-trained models in some sense "easier" to train.
**Read more:** **[Twitter thread](https://twitter.com/Hernandez_Danny/status/1357035777406853128)**
**Asya's opinion:** It's extremely cool to have a mathematical characterization of the power of pre-training. I would love to see similar analyses measuring effective data transferred for tasks other than predicting the next token -- if it turns out that modest increases in model size compensate for small datasets in a wide variety of tasks, that makes a strong case that unsupervised learning will be most of the work towards transformative abilities.
Reading these scaling papers really makes me think that there's some deeper theoretical understanding of distributions and predictive models that these results are accessing, maybe encapsulated by **[this theory paper](https://arxiv.org/abs/2004.10802)** that I still haven't read...
**Rohin's opinion:** Like Asya, I really like the simplicity of the functional form of the scaling law, and the fits to the data seem quite good. I was quite surprised that β seemed to be independent of the pretraining distribution; I would not have predicted that in advance.
Note that despite the form of the scaling law, the effective data transferred isn’t independent of the pretraining dataset size -- that dependence effectively comes through the model size N. This is because authors use compute-optimal pretraining, and so a given model size N corresponds to a specific amount of pretraining compute, which is probably almost the same as having a specific amount of pretraining data.
I am confused by the claim that distributions that are “closer” have lower α. It does make sense that for identical distributions, we should have α = 0. However, if closer distributions have lower α, and β is independent of the distribution, then as your finetuning dataset gets sufficiently large, you actually prefer the further-away distribution! For example, once your finetuning dataset hits 10 trillion points, the scaling laws predict that you prefer to have pretrained on text, rather than 50% text and 50% code, which seems really bizarre. Possibly the scaling laws break down before that point, and in any case a *finetuning* dataset of 10 trillion data points would be ridiculously massive, but it still seems like something needs to be explained here.
Could we use this to improve timelines estimates? I take a stab at a calculation **[here](https://www.lesswrong.com/posts/KrJfoZzpSDpnrv9va/draft-report-on-ai-timelines?commentId=LqZidQ6bEtDnqP6ji)**; the *very rough and uncertain* conclusion is that while transfer does seem to be a useful way to reduce compute requirements, the overall effect is not large.
TECHNICAL AI ALIGNMENT
=======================
PROBLEMS
---------
**[Challenges of Aligning Artificial Intelligence with Human Values](https://www.ies.ee/bahps/acta-baltica/abhps-8-2/04_Sutrop-2020-2-04.pdf)** *(Margit Sutrop)* (summarized by Rohin): This paper argues that since immoral humans could use AI systems to do harm, we must build ethical rules into AI systems. For this purpose, the traditional notion of “value alignment” is not enough, as it only requires that the AI system do what the user wants, which might not be ethical. But we also cannot embed a single theory of ethics into an AI system, as there is no agreement on such a theory. Instead, we should focus on what we *don’t* want an AI system to do, and *rule out* that behavior, while remaining uncertain or agnostic on what should be done.
**Rohin's opinion:** I agree that successful AI alignment does not rule out the possibility of malicious use of AI systems. This paper is proposing putting rules inside the AI system that handle this problem. But as the paper itself notes, it seems quite challenging to even figure out what rules we would want.
I personally am more optimistic about the alternate route, where we put rules *outside* the AI system to handle the problem, that is, we create laws and regulations around the use of AI, such that malicious uses can be blamed on the human operator, and enforcement mechanisms that ensure that we actually catch and punish such malicious uses.
PREVENTING BAD BEHAVIOR
------------------------
**[Challenges for Using Impact Regularizers to Avoid Negative Side Effects](https://arxiv.org/abs/2101.12509)** *(David Lindner, Kyle Matoba, and Alexander Meulemans)* (summarized by Rohin): I’m not summarizing this literature review on impact regularization because we’ve covered almost all of the ideas previously in this newsletter (e.g. **[this blog post](https://medium.com/@deepmindsafetyresearch/designing-agent-incentives-to-avoid-side-effects-e1ac80ea6107)** (**[AN #49](https://mailchi.mp/efed27be268a/alignment-newsletter-49)**)). However, I do recommend it for its short, high-level introduction to existing ideas in impact regularization, as well as its ideas for future work.
HANDLING GROUPS OF AGENTS
--------------------------
**[Norms for beneficial A.I.: A computational analysis of the societal value alignment problem](https://arxiv.org/abs/1907.03843)** *(Pedro Fernandes et al)* (summarized by Rohin): This paper presents a simple quantitative model to argue for the following two observations:
1. Unless they are willing to “fall behind” others, individual actors will need to use AI systems to stay competitive.
2. Those AI systems will optimize for their owner’s goals, even though a better outcome could be achieved if all AI systems optimized for the average welfare across all actors.
MISCELLANEOUS (ALIGNMENT)
--------------------------
**[Distinguishing claims about training vs deployment](https://www.alignmentforum.org/posts/L9HcyaiWBLYe7vXid/distinguishing-claims-about-training-vs-deployment)** *(Richard Ngo)* (summarized by Rohin): One story for AGI is that we train an AI system on some objective function, such as an objective that rewards the agent for following commands given to it by humans using natural language. We then deploy the system without any function that produces reward values; we instead give the trained agent commands in natural language. Many key claims in AI alignment benefit from more precisely stating whether they apply during training or during deployment.
For example, consider the instrumental convergence argument. The author proposes that we instead think of the training convergence thesis: a wide range of environments in which we could train an AGI will lead to the development of goal-directed behavior aimed towards certain convergent goals (such as self-preservation). This could happen either via the AGI internalizing them directly as final goals, or by the AGI learning final goals for which these goals are instrumental.
The author similarly clarifies goal specification, the orthogonality thesis, fragility of value, and Goodhart’s Law.
**[Putting the humanity into inhuman systems: How human factors and ergonomics can be used to manage the risks associated with artificial general intelligence](https://onlinelibrary.wiley.com/doi/10.1002/hfm.20883)** *(Paul M. Salmon et al)* (summarized by Rohin): This paper argues that the methods of Human Factors and Ergonomics (HFE) should be applied to AGI safety. They list fifteen different methods from the field, typically used to analyze the performance of humans in systems, which could be applied to AGI instead (on the assumption that AGI will be more like humans than like machines in today’s systems). They then give examples of how these might be applied to the Prometheus story in the prologue of **[Life 3.0](https://www.amazon.com/Life-3-0-Being-Artificial-Intelligence/dp/1101946598)**.
**Rohin's opinion:** I’m not very familiar with this field, but among other techniques the paper mentions STAMP and STPA which we’ve previously seen in **[Engineering a Safer World](https://static1.squarespace.com/static/53b78765e4b0949940758017/t/57d87eb6d2b8571af3501b26/1473898764674/Engineering_a_Safer_World+Nancy+Leveson.pdf)** (**[AN #112](https://mailchi.mp/b39cb50e2cea/an-112-engineering-a-safer-world)**). It does seem to me like these techniques would be useful to apply to the entire sociotechnical system, of which an AGI system is just one part (and this is what the paper’s examples do). It is less clear to me whether it makes sense to take techniques designed for humans and apply them to AGI: perhaps we’ll have enough understanding of the differences between humans and AGI that we could do this in a reasonable way, but I think there is a real risk that the methods give incorrect conclusions simply because they make incorrect assumptions about how AGI works (given that they were designed for humans). Nonetheless, I do agree with the core claim of this paper that HFE is worth exploring.
**[The Challenge of Value Alignment: from Fairer Algorithms to AI Safety](https://arxiv.org/abs/2101.06060)** *(Iason Gabriel et al)* (summarized by Rohin): This book chapter provides an introduction to AI alignment from a philosophical lens.
NEAR-TERM CONCERNS
===================
RECOMMENDER SYSTEMS
--------------------
**[Beyond Engagement: Aligning Algorithmic Recommendations With Prosocial Goals](https://www.partnershiponai.org/beyond-engagement-aligning-algorithmic-recommendations-with-prosocial-goals/)** *(Jonathan Stray)* (summarized by Rohin): To decide what item to show a user, a recommender system needs to have some metric by which to rank items. Since this metric must usually be automated, it often contains in large part some operationalization of “engagement”. Unfortunately, this metric may not be able to differentiate between clickbait or extremist content on the one hand, and actually valuable posts on the other. In a workshop on the topic, participants brainstormed five main approaches for improvement:
1. **Build better controls:** Offer users more and better ways to control their feed.
2. **Develop standardized survey-based metrics:** Surveys should be able to get a significantly higher quality signal to optimize than engagement.
3. **Pay users for better data,** such as survey data.
4. **Recommend feeds, not items:** If we rank items individually, it is quite likely that all the posts of the same type (e.g. controversial posts) will get high scores. By ranking entire feeds, we can also optimize for the diversity of items within the feed.
5. **Incentivize the creation of different feeds,** so that users can choose which ones they prefer all things considered.
**[What are you optimizing for? Aligning Recommender Systems with Human Values](https://participatoryml.github.io/papers/2020/42.pdf)** *(Jonathan Stray et al)* (summarized by Rohin): While the previous blog post focused on societal-level approaches to recommender systems, this paper looks at what can be done at a technical level. By analyzing existing case studies of improvements to recommender systems (some of which we’ve **[seen before](https://medium.com/@PartnershipAI/aligning-ai-to-human-values-means-picking-the-right-metrics-855859e6f047)** (**[AN #96](https://mailchi.mp/f534bdc85c58/an-96-buck-and-i-discussargue-about-ai-alignment)**)), the authors identify a typical approach taken in industry today.
First, engineers identify a problem with an already-deployed recommendation engine, perhaps from user feedback, or through monitoring. Second, they develop a concrete procedure to identify instances of this problem in the recommendations -- a typical approach is to curate a dataset and train an ML classifier to identify these instances, though it is also possible to use manual review. Finally, the recommender system is adjusted to avoid the problem, for example by adding a term to the objective when training the recommender system, or by filtering its outputs based on the classifier’s output.
The authors then propose four high-level technical approaches to recommender alignment:
1. Develop better measures of what we want out of a recommendation engine, for example, an operationalization of “well-being” rather than “engagement”.
2. Allow users to collaboratively design the recommendation engine (called *participatory design*). Rather than have a company decide on how to trade off between different objectives, allow the users to settle upon the appropriate tradeoffs themselves.
3. Interactively learn about the user’s values. While this could look like building better controls as suggested in the previous post, it could also involve e.g. using **[Inverse Reward Design](https://arxiv.org/abs/1711.02827)** (**[AN #69](https://mailchi.mp/59ddebcb3b9a/an-69-stuart-russells-new-book-on-why-we-need-to-replace-the-standard-model-of-ai)**) to maintain appropriate uncertainty over what the user cares about.
4. Design around “time well spent”, as evaluated by users on reflection or after consideration, rather than revealed preferences or immediate judgments. For example, we could show users a summary of their activity over the past month and ask how happy they are about it.
**Read more:** **[Aligning AI Optimization to Community Well-Being](https://link.springer.com/article/10.1007/s42413-020-00086-3)** (an expanded version of **[Aligning AI to Human Values means Picking the Right Metrics](https://medium.com/@PartnershipAI/aligning-ai-to-human-values-means-picking-the-right-metrics-855859e6f047)** (**[AN #96](https://mailchi.mp/f534bdc85c58/an-96-buck-and-i-discussargue-about-ai-alignment)**))
**Rohin's opinion:** Both this paper and the previous post seem like meaningful progress in ideas for making recommendation engines better (though as a caveat, I don’t follow this space and so don’t know to what extent this has been said before). I’m glad that we’re getting to the point of actually proposing technical solutions; I hope to see more papers implementing such solutions (we’ve seen one from Twitter **[recently](https://arxiv.org/abs/2008.12623)** (**[AN #123](https://mailchi.mp/62ef1fe8c13a/an-123inferring-what-is-valuable-in-order-to-align-recommender-systems)**)).
#### **FEEDBACK**
I'm always happy to hear feedback; you can send it to me, **[Rohin Shah](https://rohinshah.com/)**, by **replying to this email**.
#### **PODCAST**
An audio podcast version of the **Alignment Newsletter** is available. This podcast is an audio version of the newsletter, recorded by **[Robert Miles](http://robertskmiles.com/)**. |
93c349dd-63f2-4c83-8428-b5f999f640c8 | StampyAI/alignment-research-dataset/blogs | Blogs | For UBI
For UBI
-------
All my friends know that I'm a huge fan of *Universal Basic Income* for a variety of reasons. I'll outline here a collection of my main arguments for UBI.
First things first, I'll define UBI: it has to be Universal, it has to be Basic, and it has to be an Income.
**Universal** means that everyone (this can be reasonably restricted to *every adult citizen* of the country one is talking about implementing UBI in) must get it, regardless of employment situation. This is a very critical part: if you get a minimum wage job, you still get the UBI on top, so that it doesn't disincentivize work. It can make work *less* incentivized than before, but it can't *disincentivize* it the way many welfare programs work and create poverty traps.
**Basic** means that it must be at least enough to reasonably live, whatever that number is. If you think someone needs 1500$/mo to live, then it must be at least that. However, there is a caveat here: I don't think it's unreasonable to expect people on UBI to make more reasonable living decisions, notably such as living somewhere cheaper than they'd like.
**Income** means that it must be money, not coupons or food stamps or whatever. This is a crucial part, and is the part I consider most important to weird people and marginized groups: the less the Standard Majority Needs correspond to your needs, the less you'll get value out of being provided those; with money, instead, you're free to decide what it is you need and value.
Here are some of my favorite UBI arguments:
* **The Housing Crisis**: with UBI, people don't need to work in those giant, super-expensive cities anymore, because they don't need the jobs that are in them. UBI not only lifts a ton of people out of poverty and helps the homeless tremendously, but also lets people move out of the giant cities, thereby decreasing demand and possible making rents in those cities actually go down as a result. In addition, if UBI is a reasonable amount, it's not out of the question that people could purchase their own homes with loans paid with UBI; banks will love giving loans to people with an income that *is guaranteed to remain forever*, and eventually this could emancipate a lot of people out of depending on landlords.
* **Healthcare**: notably [in the US](https://www.youtube.com/watch?v=U1TaL7OhveM), there are reasonable arguments to be made against either a public healthcare system or a private healthcare market. With UBI, we can get the best of both worlds: make the healthcare private market, but make everyone's UBI be enough to cover, on top of other living, a reasonable private health insurance. That way, those who want to opt out can do so, insurances and health companies are still incentivized to reduce prices to an extent (or more people might just use that money on something else), but everyone is guaranteed to be *able* to afford healthcare.
* **Discrimination**: a large part of the cycle of racism (poverty → lesser education → lesser jobs → kids themselves in poverty) is the employment part. UBI not just helps by being redistributive, but also by making it okay to actually not have a job, and greatly easing the pressure poor people having with paying bills or food. If coupled with the housing crisis solution above, this could even lead to entire new integrated communities largely thriving on UBI.
* **Government corruption and lobbyism**: if they have the UBI to afford it, the poor and middle class could participate a lot more in funding political parties and maybe even lobbyists; in that sense, UBI has the potential to realign even democracy with the interests of the people.
* **Domestic abuse, etc**: all sorts of situations of this type where one party is dependent on another for money, are suddenly alleviated if both parties get free money enough to live.
* **Exploitation/poor work conditions/poor wages**: UBI gives workers the ability to just refuse employment altogether, giving them tremendous negotiating ability in the labor market. Raising the price of labor would also accelerate automation, which we should want (and which, if we have UBI, is actually fine).
* **Even Conservatives!**: with UBI, lifestyles such as the traditional nuclear family become easier to actually implement, as the wife can contribute to the family finances with her own UBI.
* **Not Enough Enterpreneurship**: a lot more people would be able to start working on projects that might actually create value, and work on those with other people, if none of them needs an external source of funding. This also covers usually less profitable prospects, like artistic careers.
* **Welfare But Better**: usual welfare systems are extremely inefficient and bureaucratically heavy. On the other hand, *just giving everyone a fixed pile of money* is extremely simple and easily implemented; with the same funding, a UBI scheme could thus result in actually a lot more money actually going to the general poor population.
* **UBI is not that far away politically**: UBI is already a fairly popular idea in the field of economics (and even in the rationalist community). Really, all we need right now to get UBI implemented is popular support, i.e. you reading this right now, being in favor of it.
But, really, these are all somehow related to the least practical but, in my opinion, most important argument:
* **The Philosophical Argument**: UBI is *philosophically* important because it makes the economy *intrinsically value people*. This importance of this cannot be stressed enough: under UBI, no longer are people valued just for their economic output in the same way any other market resource is, but people are actually *what markets become aligned to provide value for*. This is true emancipation: freedom from labor, the ability to pursue whatever it is you actually care about, without having to care about whether you can afford to survive.
Edit 2021-02-24: Another, more complete list of argument can be found [here](https://www.reddit.com/r/BasicIncome/wiki/index). |
33ba2731-5ece-45c9-bc5d-83af0bcd40ba | StampyAI/alignment-research-dataset/blogs | Blogs | Exponential and non-exponential trends in information technology
*Co-authored with Lila Rieber.*
In [*The Singularity is Near*](http://smile.amazon.com/Singularity-Near-Humans-Transcend-Biology-ebook/dp/B000QCSA7C/), Ray Kurzweil writes that “every aspect of information and information technology is growing at an exponential pace.”[1](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_0_11027 "Page 85. In the same book, he also writes that “we see ongoing exponential growth of every aspect of information technology, including price-performance, capacity, and rate of adoption.” (p. 377). In How to Create a Mind, Kurzweil writes that “In the course of my investigation, I made a startling discovery: If a technology is an information technology, the basic measures of price/performance and capacity… follow amazingly precise exponential trajectories” (p. 254).") In *[Abundance](http://www.amazon.com/Abundance-Future-Better-Than-Think-ebook/dp/B005FLOGMM/)*, the authors list eight fields — including nanomaterials, robotics, and medicine — as “exponentially growing fields.”[2](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_1_11027 "Page 57. In general, Diamandis & Kotler seem to agree with Kurzweil that all information technologies experience exponential growth curves. E.g. on page 99 they write that “Although [some agroecological] practices themselves look decidedly low tech, all the fields they’re informed by are information-based sciences and thus on exponential growth curves,” and on page 190 they write that “almost every component of medicine is now an information technology and therefore on an exponential trajectory.”") [*The Second Machine Age*](http://www.amazon.com/Second-Machine-Age-Prosperity-Technologies-ebook/dp/B00D97HPQI/) says that “technical progress” in general is “improving exponentially.”[3](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_2_11027 "Page 10. The authors also seem to expect exponential trends for anything that becomes a digital process: “…batteries… haven’t improved their performance at an exponential rate because they’re essentially chemical devices, not digital ones…” (p. 52).")
These authors are correct to emphasize that exponential trends in technological development are surprisingly common ([Nagy et al. 2013](http://www.plosone.org/article/info%3Adoi%2F10.1371%2Fjournal.pone.0052669)), and that these trends challenge the wisdom of our [built-in heuristic](http://wiki.lesswrong.com/wiki/Absurdity_heuristic) to ignore futures that *sound* absurd. (To someone in the 1980s, the iPhone is absurd. To us, it is an affordable consumer good.)
Unfortunately, these and other popular discussions of “exponential technologies” are often very succinct and therefore ambiguous, resulting in public and professional misunderstanding.[4](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_3_11027 "E.g. Kurzweil seems to use a fairly loose definition of “exponential.” For example in Kurzweil (2001) he gives this chart of ISP cost-performance as an example exponential trend. Sometimes this seems to cause confusion in dialogue. For example, in response to Ilkka Tuomi’s criticisms (2002, 2003) of claims of exponential trends in computing, Kurzweil wrote that if Tuomi were correct, “I would have to conclude that the one-quarter MIPS computer costing several million dollars that I used at MIT in 1967 and the 1000 MIPS computer that I purchased recently for $2,000 never really existed… I admire his tenacity in attempting to prove that the world of information technology is flat (i.e., linear).” But Tuomi’s views don’t entail that, and Tuomi didn’t say that trends in information technology have been linear. The conflict appears to stem from the fact that Tuomi was using “exponential” in the strict sense, while Kurzweil was using the term in a very loose sense. This becomes clearer in Tuomi’s reply to Kurzweil.") I (Luke) regularly encounter people who have read the books above and come away with the impression that all information technologies show roughly exponential trends all the time. But this isn’t true unless you have a *very* broad concept of what counts as “roughly exponential.”
So, without speculating much about what Kurzweil & company intend to claim, we’ll try to clear up some common misunderstandings about exponential technologies by showing a few examples of exponential and not-so-exponential trends in information technology. A more thorough survey of trends in information technology must be left to other investigators.[5](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_4_11027 "Our thanks to Jonah Sinick for his assistance in researching this post.")
#### Computations per dollar: still exponential
It’s clear that Kurzweil himself does not *literally* mean that “every aspect of information and information technology is growing at an exponential pace,” for he has previously discussed examples of non-exponential growth in some aspects of information technology. For example, he’s well aware that the exponential trend in processor clock speed broke down in 2004, as shown in [Fuller & Millett (2011a)](http://commonsenseatheism.com/wp-content/uploads/2014/03/Fuller-Millett-Computing-Performance-Game-Over-or-Next-Level-in-IEEE-Computer-Society.pdf):[6](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_5_11027 "It should be noted, however, that the exponential trend line for clock speed on page 61 of The Singularity is Near (2005) is now known to be incorrect. Kurzweil’s graph used the 2002 ITRS report to project the trend line for 2001-2016, but actual growth in clock speed fell substantially short of the ITRS projection.")
Because this is a logarithmic chart, a straight line represents an exponential trend. Notice that clock speed stopped improving exponentially in 2004, but transistors per chip has continued to increase exponentially via the jump from single-core to multicore processors.
Elsewhere, Kurzweil tends to emphasize exponential trends in **price-performance ratios** specifically, for example *computations per dollar*. This is perfectly reasonable. Most of us don’t care about the fine details of processor architecture — we just care about how much *stuff we can do* per dollar.[7](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_6_11027 "As Fuller & Millett (2011b) write, “When we talk about scaling computing performance, we implicitly mean to increase the computing performance that we can buy for each dollar we spend” (p. 81).") And thus far, the exponential trend in computations per dollar has kept up.[8](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_7_11027 "Kurzweil (2012), ch. 10, footnote 10 shows “calculations per second per $1,000” growing exponentially from 1900 through 2010, including several data points after 2004. However, we couldn’t find his data sources, and we don’t know whether he adjusted for inflation, so we’ve relied instead on a data set provided by Koh & Magee (2006), extended by data we pulled from NotebookCheck, PCStats, Tom’s Hardware, and CPU-World. Our raw data are here and show a continuing exponential trend in MIPS per dollar, adjusted for inflation.")
It’s unclear, however, how much longer this trend can be maintained. In particular, the [dark silicon problem](http://intelligence.org/2013/10/21/hadi-esmaeilzadeh-on-dark-silicon/) may slow the currently exponential trend in computations per dollar. Joel Hruska covers other recent challenges to the trend [here](http://www.extremetech.com/computing/178529-this-is-what-the-death-of-moores-law-looks-like-euv-paused-indefinitely-450mm-wafers-halted-and-no-path-beyond-14nm), including the halted production of the 450mm wafers that Intel, TSMC, and Samsung all [bet their money on](http://www.extremetech.com/computing/132604-intel-invests-in-asml-to-boost-extreme-uv-lithography-massive-450mm-wafers) 18 months ago.
#### DRAM capacity per dollar: a slowing trend
Another important price-performance trend is *DRAM capacity per dollar*. This trend was almost precisely exponential for many years but recently the trend has slowed:[9](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_8_11027 "This chart uses data from Bryant & O’Hallaron (2011), p. 584 and from the Performance Curve Database. Raw data here.")
[](https://intelligence.org/wp-content/uploads/2014/04/DRAM-chart-2.png)
The same slowing trend for DRAM is also reported in [Hennessy & Patterson (2011)](http://www.amazon.com/Computer-Architecture-Quantitative-Approach-Kaufmann-ebook/dp/B0067KU84U/), on page 17. On page 100 they remark:
> DRAMs obeyed Moore’s law for 20 years, bringing out a new chip with four times the capacity every three years. Due to the manufacturing challenges of a single-bit DRAM, new chips only double capacity every two years since 1998. In 2006, the pace slowed further, with the four years from 2006 to 2010 seeing only a [single] doubling of capacity.
>
>
#### SRAM capacity per dollar: a slowing trend
What about another kind of computer memory, like [SRAM](http://en.wikipedia.org/wiki/Static_random-access_memory)? The cost of SRAM dropped precipitously from 1980 to 1990 but has dropped more slowly since then.[10](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_9_11027 "Data from Bryant & O’Hallaron (2011), p. 584. Raw data here.")
[](https://intelligence.org/wp-content/uploads/2014/04/SRAM-chart-2.png)
#### Hard drive capacity per dollar: interrupted by floods in Thailand
Cost per gigabyte of hard drive storage had been dropping exponentially for about 30 years when suddenly hard drive prices actually [*increased*](http://www.computerworld.com/s/article/9227829/Hard_drive_prices_to_remain_high_until_2014) for a while because [October 2011 floods in Thailand](http://en.wikipedia.org/wiki/2011_Thailand_floods#Damages_to_industrial_estates_and_global_supply_shortages) destroyed some hard drive factories. Hard drive prices have been comparatively flat since then:[11](https://intelligence.org/2014/05/12/exponential-and-non-exponential/#footnote_10_11027 "Our data are drawn from Matthew Komorowski’s page on storage cost (but adjusted for inflation), Koh & Magee (2006), Bryant & O’Hallaron (2011), and the Performance Curve Database.")
[](https://intelligence.org/wp-content/uploads/2014/04/Hard-drive-storage-cost.png)
The floods hurt many computing providers, who struggled (and sometimes failed) to offer services at the low prices they had anticipated based on exponential expectations: see e.g. the comments by [BackBlaze](http://blog.backblaze.com/2013/11/26/farming-hard-drives-2-years-and-1m-later/), [Intel](http://money.cnn.com/2011/12/12/technology/intel_earnings_revision/index.htm), and [Joyent](http://gigaom.com/2011/12/27/what-the-hdd-shortage-means-for-cloud-computing/).
Whereas the exponential trend for processor clock speed was brought to a halt by physics, the exponential trend in cost per gigabyte of storage was slowed (at least for now) by natural disaster.
---
1. Page 85. In the same book, he also writes that “we see ongoing exponential growth of every aspect of information technology, including price-performance, capacity, and rate of adoption.” (p. 377). In [*How to Create a Mind*](http://smile.amazon.com/How-Create-Mind-Thought-Revealed-ebook/dp/B007V65UUG/), Kurzweil writes that “In the course of my investigation, I made a startling discovery: If a technology is an information technology, the basic measures of price/performance and capacity… follow amazingly precise exponential trajectories” (p. 254).
2. Page 57. In general, Diamandis & Kotler seem to agree with Kurzweil that all information technologies experience exponential growth curves. E.g. on page 99 they write that “Although [some agroecological] practices themselves look decidedly low tech, all the fields they’re informed by are information-based sciences and thus on exponential growth curves,” and on page 190 they write that “almost every component of medicine is now an information technology and therefore on an exponential trajectory.”
3. Page 10. The authors also seem to expect exponential trends for anything that becomes a digital process: “…batteries… haven’t improved their performance at an exponential rate because they’re essentially chemical devices, not digital ones…” (p. 52).
4. E.g. Kurzweil seems to use a fairly loose definition of “exponential.” For example in [Kurzweil (2001)](http://www.kurzweilai.net/the-law-of-accelerating-returns) he gives [this chart](https://intelligence.org/wp-content/uploads/2014/03/ISP-cost-performance.jpg) of ISP cost-performance as an example exponential trend. Sometimes this seems to cause confusion in dialogue. For example, in response to Ilkka Tuomi’s criticisms ([2002](http://firstmonday.org/ojs/index.php/fm/article/viewArticle/1000/921), [2003](http://meaningprocessing.com/personalPages/tuomi/articles/Kurzweil.pdf)) of claims of exponential trends in computing, Kurzweil [wrote](http://www.kurzweilai.net/exponential-growth-an-illusion-response-to-ilkka-tuomi) that if Tuomi were correct, “I would have to conclude that the one-quarter MIPS computer costing several million dollars that I used at MIT in 1967 and the 1000 MIPS computer that I purchased recently for $2,000 never really existed… I admire his tenacity in attempting to prove that the world of information technology is flat (i.e., linear).” But Tuomi’s views don’t entail that, and Tuomi didn’t say that trends in information technology have been linear. The conflict appears to stem from the fact that Tuomi was using “exponential” in the strict sense, while Kurzweil was using the term in a very loose sense. This becomes clearer in Tuomi’s [reply to Kurzweil](http://www.meaningprocessing.com/personalPages/tuomi/articles/ResponseToKurzweil.pdf).
5. Our thanks to Jonah Sinick for his assistance in researching this post.
6. It should be noted, however, that the exponential trend line for clock speed on page 61 of *The Singularity is Near* (2005) is now known to be incorrect. Kurzweil’s graph used the [2002 ITRS report](http://www.itrs.net/Links/2006Update/2006UpdateFinal.htm) to project the trend line for 2001-2016, but actual growth in clock speed fell substantially short of the ITRS projection.
7. As [Fuller & Millett (2011b)](http://www.amazon.com/The-Future-Computing-Performance-Level/dp/0309159512/) write, “When we talk about scaling computing performance, we implicitly mean to increase the computing performance that we can buy for each dollar we spend” (p. 81).
8. [Kurzweil (2012)](http://www.amazon.com/How-Create-Mind-Thought-Revealed/dp/0670025291/), ch. 10, footnote 10 shows “calculations per second per $1,000” growing exponentially from 1900 through 2010, including several data points after 2004. However, we couldn’t find his data sources, and we don’t know whether he adjusted for inflation, so we’ve relied instead on a data set provided by [Koh & Magee (2006)](http://web.mit.edu/cmagee/www/documents/15-koh_magee-tfsc_functional_approach_studying_technological_progress_vol73p1061-1083_2006.pdf), extended by data we pulled from [NotebookCheck](http://www.notebookcheck.net/), [PCStats](http://pcstats.com/), [Tom’s Hardware](http://www.tomshardware.com/), and [CPU-World](http://www.cpu-world.com/). Our raw data are [here](https://docs.google.com/spreadsheets/d/1JIYhJ3QPrP0VUlhwVZ5uPnRnBfTs8I_H4CH0XHJR2XA/edit?usp=sharing) and show a continuing exponential trend in MIPS per dollar, adjusted for inflation.
9. This chart uses data from [Bryant & O’Hallaron (2011)](http://www.amazon.com/Computer-Systems-Programmers-Perspective-2nd-ebook/dp/B008VIXMWQ/), p. 584 and from the [Performance Curve Database](http://pcdb.santafe.edu/graph.php?curve=25). Raw data [here](https://docs.google.com/spreadsheets/d/1i91c82nRczN8DTbs21J8IiZYI_EKAafCR-Ny1qVDyq0/edit?usp=sharing).
10. Data from [Bryant & O’Hallaron (2011)](http://www.amazon.com/Computer-Systems-Programmers-Perspective-2nd-ebook/dp/B008VIXMWQ/), p. 584. Raw data [here](https://docs.google.com/spreadsheets/d/14k-PP-ojAqzRz2VT19gjlAAwA9iYMdR7ILJ1EnnXJiI/edit?usp=sharing).
11. [Our data](https://docs.google.com/spreadsheets/d/1JwaZaQeuos0-YW8VF3RjhqmWXceggkswQk3KJtzKVW8/edit?usp=sharing) are drawn from Matthew Komorowski’s [page on storage cost](http://www.mkomo.com/cost-per-gigabyte-update) (but adjusted for inflation), [Koh & Magee (2006](http://web.mit.edu/cmagee/www/documents/15-koh_magee-tfsc_functional_approach_studying_technological_progress_vol73p1061-1083_2006.pdf)), [Bryant & O’Hallaron (2011)](http://www.amazon.com/Computer-Systems-Programmers-Perspective-2nd-ebook/dp/B008VIXMWQ/), and the [Performance Curve Database](http://pcdb.santafe.edu/graph.php?curve=24).
The post [Exponential and non-exponential trends in information technology](https://intelligence.org/2014/05/12/exponential-and-non-exponential/) appeared first on [Machine Intelligence Research Institute](https://intelligence.org). |
a902fd3f-7e3c-4fdb-a714-444eb228fae4 | trentmkelly/LessWrong-43k | LessWrong | OpenAI's Sora is an agent
If you haven't already, take a look at Sora, OpenAI's new text-to-video AI. Sora can create scarily-realistic videos of nearly any subject. Unlike previous state-of-the-art AIs, the videos are coherent across time scales as long as one minute, and they can be much more complex.
Looking through OpenAI's research report, this one section caught my attention:
For a moment, I was confused: "what does it mean, Sora can 'control the player in Minecraft with a basic policy?' It's generating footage of a video game, not actually playing it... right?"
It's true that in these particular demo videos, Sora is "controlling the player" in its own internal model, rather than interfacing with Minecraft itself. However, I believe OpenAI is hinting that Sora can open the door to a much broader set of applications than just generating video.
In this post, I'll sketch an outline of how Sora could be used as an agent that plays any video game. With a bit of "visual prompt engineering," I believe this would even be possible with zero modifications to the base model. You could easily improve the model's efficiency and reliability by fine-tuning it and adding extra types of tokens, but I'll refrain from writing about that here.
The capabilities I'm predicting here aren't totally novel - OpenAI itself actually trained an AI to do tasks in Minecraft, very similarly to what I'll describe here.
What interests me is that Sora will likely be able to do many general tasks without much or any specialized training. In much the same way that GPT-3 learned all kinds of unexpected emergent capabilities just by learning to "predict the next token," Sora's ability to accurately "predict the next frame" could let it perform many visual tasks that depend on long-term reasoning.
Sorry if this reads like an "advancing capabilities" kind of post. Based on some of the wording throughout their research report, I believe OpenAI is already well aware of this, and it would be better for people to understan |
0886abbf-440e-42f6-923e-2e0617eaceae | trentmkelly/LessWrong-43k | LessWrong | Meetup : Irvine Meetup Wednesday August 31
Discussion article for the meetup : Irvine Meetup Wednesday August 31
WHEN: 31 August 2011 06:00:00PM (-0700)
WHERE: 4187 Campus Dr, University Center, Irvine, CA 92612
This continues the weekly meetups in Irvine. As always the meetup at the outdoor food court in the University Center near UCI, from 6:00 to 8:00 (or whenever we actually decide to leave). Look for the sign with naive neural classifiers for bleggs and rubes. See also the email group and calendar for the Southern California Meetup Group
Discussion article for the meetup : Irvine Meetup Wednesday August 31 |
70e31226-2d28-4223-b54b-d246d1129a79 | trentmkelly/LessWrong-43k | LessWrong | Bayeswatch 8: Antimatter
Vi woke up to the sound of Miriam disassembling the scout's control system.
"Please tell me you're not scuttling our ride home," said Vi.
"I'm not scuttling our ride home. Vaccinate yourself in case this leads to another Z-Day," said Miriam.
The suitcase was labeled with an orthonormal cube Vi recognized from her training as the Mark of Pandora. Vi opened the suitcase. One half contained vials, syringes and needles. The other half contained a nest of wires, circuitboards and heatsinks wrapped around a slab of computronium. She injected the vaccine into her upper arm muscle.
"You didn't tell me what you're doing," said Vi.
Miriam tossed Vi a sphere the size of a golf ball. It was coated in depleted uranium. "This is a neutrino beacon. It can be remotely activated. Well, technically it's an anti-neutrino beacon. But we call them neutrino beacons. It's not like matter neutrinos are used in your microwave oven."
"We've been flying around with an antimatter bomb?" said Vi.
"We've been flying around with a harmless antimatter bomb. Neutrinos barely interact with regular matter. Covert Bayeswatch teams use these to signal for rescue from hostile territory. Bayeswatch's sensor array could detect us if they chose to remotely activate it," said Miriam.
"Just Bayeswatch?" said Vi.
"A global neutrino triangulator sensitive enough to detect one of these is beyond the purchasing power of mere nation-states," said Miriam.
"Speaking of countries, do you have any idea who or where our enemy is?" said Vi.
"They can't be anywhere with a Bayeswatch-backed police state. They're not from China, Russia, Western Europe, the United States or anyone else in the Alliance. Our enemy has to be somewhere with significant high-tech industrial capacity. We can cross out the Philippines, Mozambique and Vietnam," said Miriam.
"Taiwan then? Or Singapore?" said Vi.
"Maybe. They could be based out of Argentina, Brazil or South Africa. We just don't have enough information," said Miriam.
" |
fb565030-0871-4ac7-85fe-86621d829998 | trentmkelly/LessWrong-43k | LessWrong | New LW Meetups: Prague, Hasselt
This summary was posted to LW Main on September 26th. The following week's summary is here.
New meetups (or meetups with a hiatus of more than a year) are happening in:
* Czech's first Meetup Prague: 26 September 2014 07:30PM
* Hasselt Meetup: Brussels moves to Hasselt this month!: 11 October 2014 01:00PM
Irregularly scheduled Less Wrong meetups are taking place in:
* Atlanta September Meetup - Self Awareness: 27 September 2014 07:00PM
* Bratislava: 29 September 2014 06:00PM
* Copenhagen September Social Meetup - Botanisk Have: 27 September 2014 02:30PM
* Frankfurt: How to improve your life: 28 September 2014 02:00PM
* Houston, TX: 18 October 2014 02:00PM
* Perth, Australia: Games night: 07 October 2014 06:00PM
* Urbana-Champaign: The Steep Approach to Crazytown: 28 September 2014 02:00PM
* Utrecht: Effective Altruism and Politics: 05 October 2014 02:00PM
* Utrecht: Artificial Intelligence: 19 October 2014 02:00PM
* Utrecht: Climate Change: 02 November 2014 03:00PM
The remaining meetups take place in cities with regular scheduling, but involve a change in time or location, special meeting content, or simply a helpful reminder about the meetup:
* Austin, TX: 27 September 2025 01:30PM
* London social meetup: 28 September 2014 02:00PM
* Moscow Meetup: Unusual as usual: 28 September 2014 02:00PM
* Vienna - Superintelligence: 27 September 2014 03:00PM
* Washington DC EA meetup / Petrov day dinner: 26 September 2014 07:00PM
* Washington, D.C.: Book Swap: 28 September 2014 03:00PM
* West LA—The Worst Argument in the World: 01 October 2014 07:00PM
Locations with regularly scheduled meetups: Austin, Berkeley, Berlin, Boston, Brussels, Buffalo, Cambridge UK, Canberra, Columbus, London, Madison WI, Melbourne, Moscow, Mountain View, New York, Philadelphia, Research Triangle NC, Seattle, Sydney, Toronto, Vienna, Washington DC, Waterloo, and West Los Angeles. There's also a 24/7 online study hall for coworking LWers.
If you'd like to talk with other LW- |
692447ae-2cee-4db2-b502-a6d5eeafd1c8 | trentmkelly/LessWrong-43k | LessWrong | Internal Double Crux: Video Games
Inspired by Jacob Falkovich's Internal Diet Crux.
Disputants: Read Bermudez, and Play On.
PO: State your hypothesis, sir!
RB: You are spending too much time playing video games. Now yours.
PO: You're mistaken; I'm indulging in a reasonable amount of downtime.
RB: Using the Sapience Spell, I summon, and precommit to engaging with, the sensation of loving-kindness for whatever claims you may make or emotional disclosures you reveal. You want what's best for SupposedlyFun.
PO: Using the Sapience Spell, I summon, and precommit to engaging with, the sensation of loving-kindness for whatever claims you may make or emotional disclosures you reveal. You want what's best for SupposedlyFun.
RB: Okay. We are working four hours per day as a lawyer. This is about 65% of the daily work we were doing before we moved to a foreign country to be with our spouse who temporarily works there. We should have a lot of slack for other intellectual projects. I want us to read Bermudez' cognitive science textbook. Kahneman and Tversky can come later. We should be able to set aside 30 minutes per day for this.
PO: Nothing you said is unreasonable. But I like playing video games, and it's not abnormal for people to spend 2 hours a day on leisure pursuits. The average American apparently spends twice that time on TV per day. I, meaning you, have never been the kind of person who can just work nonstop all day. Additionally, we are still living in quarantine society, a once-per-generation if not rarer level of interference with normal life, in particular with things that keep us from getting depressed, like socializing.
RB: That's all true. However, you are able to work at the food court with the big sunny windows, or likewise at the library, and be around people while working and getting sun-eye exposure time. You could add 30 minutes of Bermudez at the end.
PO: After two hours of working, we need a substantial break[, and reading a textbook doesn't feel like a break, even tho |
4b03f38a-c825-4b49-ac5a-1dc43540531b | trentmkelly/LessWrong-43k | LessWrong | From free-energy to embodied valuing: weighted active inference in everyday life
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1d916bf1-1e7e-4843-9580-b5085670c6f4 | trentmkelly/LessWrong-43k | LessWrong | Steelmanning Inefficiency
When considering writing a hypothetical apostasy or steelmanning an opinion I disagreed with, I looked around for something worthwhile, both for me to write and others to read. Yvain/Scott has already steelmanned Time Cube, which cannot be beaten as an intellectual challenge, but probably didn't teach us much of general use (except in interesting dinner parties). I wanted something hard, but potentially instructive.
So I decided to steelman one of the anti-sacred cows (sacred anti-cows?) of this community, namely inefficiency. It was interesting to find that it was a little easier than I thought; there are a lot of arguments already out there (though they generally don't come out explicitly in favour of "inefficiency"), it was a question of collecting them, stretching them beyond their domains of validity, and adding a few rhetorical tricks.
The strongest argument
Let's start strong: efficiency is the single most dangerous thing in the entire universe. Then we can work down from that:
A superintelligent AI could go out of control and optimise the universe in ways that are contrary to human survival. Some people are very worried about this; you may have encountered them at some point. One big problem seems to be that there is no such thing as a "reduced impact AI": if we give a superintelligent AI a seemingly innocuous goal such as "create more paperclips", then it would turn the entire universe into paperclips. Even if it had a more limited goal such as "create X paperclips", then it would turn the entire universe into redundant paperclips, methods for counting the paperclips it has, or methods for defending the paperclips it has - all because these massive transformations allow it to squeeze just a little bit more expected utility from the universe.
The problem is one of efficiency: of always choosing the maximal outcome. The problem would go away if the AI could be content with almost accomplishing its goal, or of being almost certain that its goal was acc |
acb46b68-4126-4be2-89a0-a5fd1ddf8d54 | trentmkelly/LessWrong-43k | LessWrong | Sparse Autoencoders: Future Work
Mostly my own writing, except for the 'Better Training Methods' section which was written by @Aidan Ewart.
We made a lot of progress in 4 months working on Sparse Autoencoders, an unsupervised method to scalably find monosemantic features in LLMs, but there's still plenty of work to do. Below I (Logan) give both research ideas, as well as my current, half-baked thoughts on how to pursue them.
Find All the Circuits!
1. Truth/Deception/Sycophancy/Train-Test distinction/[In-context Learning/internal Optimization]
1. Find features relevant for these tasks. Do they generalize better than baselines?
2. For internal optimization, can we narrow this down to a circuit (using something like causal scrubbing) and retarget the search?
2. Understand RLHF
1. Find features for preference/reward models that make the reward large or very negative.
2. Compare features of models before & after RLHF
3. Adversarial Attacks
1. What features activate on adversarial attacks? What features feed into those?
2. Develop adversarial attacks, but only search over dictionary features
4. Circuits Across Time
1. Using a model w/ lots of checkpoints like Pythia, we can see feature & circuit formation across time given datapoints.
5. Circuits Across Scale
1. Pythia models are trained on the same data, in the same order but range in model sizes from 70M params to 13B.
6. Turn LLMs into code
1. Link to very rough draft of the idea I (Logan) wrote in two days
7. Mechanistic Anomaly Detection
1. If distribution X has features A,B,C activate, and distribution Y has features B,C,D, you may be able to use this discrete property to get a better ROC curve than strictly continuous methods.
2. How do the different operationalizations of distance between discrete features compare against each other?
8. Activation Engineering
1. Use feature directions found by the dictionary instead of examples. I predict this will generalize better, but would be good |
b60eba5b-83e8-4aa2-b9c8-fb80b3a935dd | trentmkelly/LessWrong-43k | LessWrong | Raphaël Millière on Generalization and Scaling Maximalism
I interviewed Raphaël Millière, a Presidential Scholar in Society and Neuroscience at Columbia University about his critic of “scaling maximalism” and his takes on AGI. This is part of an on-going effort where I talk to people who are skeptical of existential risk from AI so that everyone could better steelman their arguments (cf. why you might want to talk to skeptics).
Why I Interviewed Raphaël
Although we disagree on most topics, Raphaël follows closely current state of the art research in deep learning, is impressed by current advances, yet still completely disregards existential risk from AI. The reasons for his (supposedly contradictory) beliefs are related to the potential limitations of deep learning in terms of understanding, compositionality and generalization, which are shared by popular AI skeptics such as Gary Marcus or François Chollet.
Below are some quotes of Raphaël said during his interview. You can find them in full context here.
Three levels of Generalization, the Wozniak Test
> Maybe one distinction that's helpful there, is again from François Chollet's paper on the measure of intelligence, which I quite like, is this distinction between, I think it distinguishes between three levels of generalization.
>
> * So you have local generalization, which is a narrow form of generalization that pretends to generalize to known unknowns. So within a specific task. So that can be just, for example, you have a classifier that classifies pictures of dogs and cats, and then you can generalize to unseen examples, at test time, that it hasn't seen during training. So that's local generalization is just within domain known unknowns in a specific task.
> * Then there is what he calls broad generalization, that's generalizing to unknown unknowns within a broad range of tasks. So the examples he gives there would be level five self-driving or there was the Wozniak test, which was proposed by Steve Wozniak, which is building a system that can walk into a ro |
d675f77a-8c48-40c6-b64d-3ce0910c6f1b | StampyAI/alignment-research-dataset/blogs | Blogs | Three Major Singularity Schools
I’ve noticed that Singularity discussions seem to be splitting up into three major schools of thought: Accelerating Change, the Event Horizon, and the Intelligence Explosion.
* **Accelerating Change:**
+ *Core claim:* Our intuitions about change are linear; we expect roughly as much change as has occurred in the past over our own lifetimes. But technological change feeds on itself, and therefore accelerates. Change today is faster than it was 500 years ago, which in turn is faster than it was 5000 years ago. Our recent past is not a reliable guide to how much change we should expect in the future.
+ *Strong claim:* Technological change follows smooth curves, typically exponential. Therefore we can predict with fair precision when new technologies will arrive, and when they will cross key thresholds, like the creation of Artificial Intelligence.
+ *Advocates:* Ray Kurzweil, Alvin Toffler(?), John Smart
* **Event Horizon:**
+ *Core claim:* For the last hundred thousand years, humans have been the smartest intelligences on the planet. All our social and technological progress was produced by human brains. Shortly, technology will advance to the point of improving on human intelligence (brain-computer interfaces, Artificial Intelligence). This will create a future that is weirder by far than most science fiction, a difference-in-kind that goes beyond amazing shiny gadgets.
+ *Strong claim:* To know what a superhuman intelligence would do, you would have to be at least that smart yourself. To know where Deep Blue would play in a chess game, you must play at Deep Blue’s level. Thus the future after the creation of smarter-than-human intelligence is absolutely unpredictable.
+ *Advocates:* Vernor Vinge
* **Intelligence Explosion:**
+ *Core claim:* Intelligence has always been the source of technology. If technology can *significantly* improve on human intelligence – create minds smarter than the smartest existing humans – then this closes the loop and creates a positive feedback cycle. What would humans with brain-computer interfaces do with their augmented intelligence? One good bet is that they’d design the next generation of brain-computer interfaces. Intelligence enhancement is a classic tipping point; the smarter you get, the more intelligence you can apply to making yourself even smarter.
+ *Strong claim:* This positive feedback cycle goes FOOM, like a chain of nuclear fissions gone critical – each intelligence improvement triggering an average of >1.000 further improvements of similar magnitude – though not necessarily on a smooth exponential pathway. Technological progress drops into the characteristic timescale of transistors (or super-transistors) rather than human neurons. The ascent rapidly surges upward and creates *superintelligence* (minds orders of magnitude more powerful than human) before it hits physical limits.
+ *Advocates:* I. J. Good, Eliezer Yudkowsky
The thing about these three *logically distinct* schools of Singularity thought is that, while all three core claims support each other, all three strong claims tend to contradict each other.
If you extrapolate our existing version of Moore’s Law past the point of smarter-than-human AI to make predictions about 2099, then you are contradicting both the strong version of the Event Horizon (which says you can’t make predictions because you’re trying to outguess a transhuman mind) and the strong version of the Intelligence Explosion (because progress will run faster once smarter-than-human minds and nanotechnology drop it into the speed phase of transistors).
I find it very annoying, therefore, when these three schools of thought are mashed up into Singularity paste. [Clear thinking requires making distinctions.](http://www.overcomingbias.com/2007/08/the-virtue-of-n.html)
But what is still more annoying is when someone reads a blog post about a newspaper article about the Singularity, comes away with *none* of the three interesting theses, and spontaneously reinvents the dreaded fourth meaning of the Singularity:
* **Apocalyptism:** Hey, man, have you heard? There’s this bunch of, like, crazy nerds out there, who think that some kind of unspecified huge nerd thing is going to happen. What a bunch of wackos! It’s geek religion, man.
I’ve heard (many) other definitions of the Singularity attempted, but I usually find them to lack separate premises and conclusions. For example, the old Extropian FAQ used to define the “Singularity” as the Inflection Point, “the time when technological development will be at its fastest” and just before it starts slowing down. But what makes this an interesting point in history apart from its definition? What are the consequences of this assumption? To qualify as a school of thought or even a thesis, one needs an internal structure of argument, not just a definition.
If you’re wondering which of these is the *original* meaning of the term “Singularity,” it is the Event Horizon thesis of Vernor Vinge, who coined the word.
The post [Three Major Singularity Schools](https://intelligence.org/2007/09/30/three-major-singularity-schools/) appeared first on [Machine Intelligence Research Institute](https://intelligence.org). |
d5e8b752-9364-42a0-8c3a-74acb60646f8 | StampyAI/alignment-research-dataset/blogs | Blogs | Why Would AI "Aim" To Defeat Humanity?
*Click lower right to download or find on Apple Podcasts, Spotify, Stitcher, etc.*
I’ve [argued](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/) that AI systems could defeat all of humanity combined, if (for whatever reason) they were directed toward that goal.
Here I’ll explain why I think they might - in fact - end up directed toward that goal. Even if they’re built and deployed with good intentions.
In fact, I’ll argue something a bit stronger than that they *might* end up aimed toward that goal. I’ll argue that **if today’s AI development methods lead directly to powerful enough AI systems, disaster is *likely***[1](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn1) ***by default* (in the absence of specific countermeasures).**
Unlike other discussions of the AI alignment problem,[3](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn3) this post will discuss the likelihood[4](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn4) of AI systems *defeating all of humanity* (not more general concerns about AIs being misaligned with human intentions), while aiming for plain language, conciseness, and accessibility to laypeople, and focusing on modern AI development paradigms. I make no claims to originality, and list some key sources and inspirations in a footnote.[5](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn5)
Summary of the piece:
**My basic assumptions.** I assume the world could develop extraordinarily powerful AI systems in the coming decades. I previously examined this idea at length in the [most important century](https://www.cold-takes.com/most-important-century/) series.
Furthermore, in order to simplify the analysis:
* I assume that such systems will be developed using methods similar to today’s leading AI development methods, and in a world that’s otherwise similar to today’s. (I call this [nearcasting](https://www.alignmentforum.org/posts/Qo2EkG3dEMv8GnX8d/ai-strategy-nearcasting).)
* I assume that AI companies/projects race forward to build powerful AI systems, without specific attempts to prevent the problems I discuss in this piece. Future pieces will relax this assumption, but I think it is an important starting point to get clarity on what the default looks like.
**AI “aims.”** I talk a fair amount about why we might think of AI systems as “aiming” toward certain states of the world. I think this topic causes a lot of confusion, because:
* Often, when people talk about AIs having goals and making plans, it sounds like they’re overly anthropomorphizing AI systems - as if they expect them to have human-like motivations and perhaps [evil grins](https://media.npr.org/assets/img/2015/06/30/tr-09117-df20f2f4f05817e574b879d22e607f952cf87867-s1100-c50.jpg). This can make the whole topic sound wacky and out-of-nowhere.
* But I think there are good reasons to expect that AI systems will “aim” for particular states of the world, much like a chess-playing AI “aims” for a checkmate position - making choices, calculations and even *plans* to get particular types of outcomes. For example, people might want AI assistants that can creatively come up with unexpected ways of accomplishing whatever goal they’re given (e.g., “Get me a great TV for a great price”), even in some cases manipulating other humans (e.g., by negotiating) to get there. This dynamic is core to the risks I’m most concerned about: I think something that *aims* for the wrong states of the world is much more dangerous than something that just does incidental or accidental damage.
**Dangerous, unintended aims.** I’ll examine what sorts of aims AI systems might end up with, if we use AI development methods like today’s - essentially, “training” them via trial-and-error to accomplish ambitious things humans want.
* Because we ourselves will often be misinformed or confused, we will sometimes give *negative* reinforcement to AI systems that are actually acting in our best interests and/or giving accurate information, and *positive* reinforcement to AI systems whose behavior *deceives* us into thinking things are going well. This means we will be, unwittingly, training AI systems to deceive and manipulate us.
+ The idea that AI systems could “deceive” humans - systematically making choices and taking actions that cause them to misunderstand what’s happening in the world - is core to the risk, so I’ll elaborate on this.* For this and other reasons, powerful AI systems will likely end up with aims other than the ones we intended. Training by trial-and-error is slippery: the positive and negative reinforcement we give AI systems will probably not end up training them just as we hoped.
* If powerful AI systems have aims that are both unintended (by humans) and ambitious, this is dangerous. Whatever an AI system’s unintended aim:
+ Making sure it can’t be turned off is likely helpful in accomplishing the aim.
+ Controlling the whole world is useful for just about any aim one might have, and I’ve argued that advanced enough AI systems would be able to [gain power over all of humanity](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/).
+ Overall, **we should expect disaster if we have AI systems that are both (a) [powerful enough](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/) to defeat humans and (b) aiming for states of the world that we didn’t intend.**
**Limited and/or ambiguous warning signs.** The risk I’m describing is - by its nature - hard to observe, for similar reasons that a risk of a (normal, human) coup can be hard to observe: the risk comes from actors that can and will engage in *deception*, finding whatever behaviors will hide the risk. If this risk plays out, I do think we’d see *some* warning signs - but they could easily be confusing and ambiguous, in a fast-moving situation where there are lots of incentives to build and roll out powerful AI systems, as fast as possible. Below, I outline how this dynamic could result in disaster, even with companies encountering a number of warning signs that they try to respond to.
**FAQ.** An appendix will cover some related questions that often come up around this topic.
* How could AI systems be “smart” enough to defeat all of humanity, but “dumb” enough to pursue the various silly-sounding “aims” this piece worries they might have? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#how-could-ai-systems-be-smart)* If there are lots of AI systems around the world with different goals, could they balance each other out so that no one AI system is able to defeat all of humanity? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#if-there-are-lots-of-ai-systems)* Does this kind of AI risk depend on AI systems’ being “conscious”?[More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#does-this-kind-of-ai-risk-depend)* How can we get an AI system “aligned” with humans if we can’t agree on (or get much clarity on) what our values even are? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#how-can-we-get-an-ai-system-aligned)* How much do the arguments in this piece rely on “trial-and-error”-based AI development? What happens if AI systems are built in another way, and how likely is that? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#how-much-do-the-arguments-in-this-piece-rely)* Can we avoid this risk by simply never building the kinds of AI systems that would pose this danger? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#can-we-avoid-this-risk-by-simply-never-building)* What do others think about this topic - is the view in this piece something experts agree on? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#what-do-others-think-about-this-topic)* How “complicated” is the argument in this piece? [More](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#how-complicated-is-the-argument)
Starting assumptions
--------------------
I’ll be making a number of assumptions that some readers will find familiar, but others will find very unfamiliar.
Some of these assumptions are based on arguments I’ve already made (in the [most important century](https://www.cold-takes.com/most-important-century/) series). Some are for the sake of simplifying the analysis, for now (with more nuance coming in future pieces).
Here I’ll summarize the assumptions briefly, and you can **click to see more** if it isn’t immediately clear what I’m assuming or why.
**“Most important century” assumption: we’ll soon develop very powerful AI systems, along the lines of what I previously called [PASTA](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/).** (Click to expand)
In the [most important century](https://www.cold-takes.com/most-important-century/) series, I argued that the 21st century could be the most important century ever for humanity, via the development of advanced AI systems that could dramatically speed up scientific and technological advancement, getting us more quickly than most people imagine to a deeply unfamiliar future.
I focus on a hypothetical kind of AI that I call [PASTA](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/), or Process for Automating Scientific and Technological Advancement. PASTA would be AI that can essentially **automate all of the human activities needed to speed up scientific and technological advancement.**
Using a [variety of different forecasting approaches](https://www.cold-takes.com/where-ai-forecasting-stands-today/), I argue that PASTA seems more likely than not to be developed this century - and there’s a decent chance (more than 10%) that we’ll see it within 15 years or so.
I argue that the consequences of this sort of AI could be enormous: an [explosion in scientific and technological progress](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/#explosive-scientific-and-technological-advancement). This could get us more quickly than most imagine to a radically unfamiliar future.
I’ve also [argued](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/) that AI systems along these lines could defeat all of humanity combined, if (for whatever reason) they were aimed toward that goal.
For more, see the [most important century](https://www.cold-takes.com/most-important-century/) landing page. The series is available in many formats, including audio; I also provide a summary, and links to podcasts where I discuss it at a high level.
**“Nearcasting” assumption: such systems will be developed in a world that’s otherwise similar to today’s.** (Click to expand)
It’s hard to talk about risks from [transformative AI](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/) because of the many uncertainties about when and how such AI will be developed - and how much the (now-nascent) field of “AI safety research” will have grown by then, and how seriously people will take the risk, etc. etc. etc. So maybe it’s not surprising that [estimates of the “misaligned AI” risk range from ~1% to ~99%](https://www.cold-takes.com/making-the-best-of-the-most-important-century/#open-question-how-hard-is-the-alignment-problem).
This piece takes an approach I call **[nearcasting](https://www.alignmentforum.org/posts/Qo2EkG3dEMv8GnX8d/ai-strategy-nearcasting)**: trying to answer key strategic questions about transformative AI, under the assumption that such AI arrives in a world that is otherwise relatively similar to today's.
You can think of this approach like this: “Instead of asking where our ship will ultimately end up, let’s start by asking what destination it’s pointed at right now.”
That is: instead of trying to talk about an uncertain, distant future, we can talk about the easiest-to-visualize, closest-to-today situation, and how things look there - and *then* ask how our picture might be off if other possibilities play out. (As a bonus, it doesn’t seem out of the question that transformative AI will be developed extremely soon - 10 years from now or faster.[6](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn6) If that’s the case, it’s especially urgent to think about what that might look like.)
**“Trial-and-error” assumption: such AI systems will be developed using** **techniques broadly in line with how most AI research is done today, revolving around black-box trial-and-error.** (Click to expand)
What I mean by “black-box trial-and-error” is explained briefly in an [old Cold Takes post](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/#making-pasta), and in more detail in more technical pieces by [Ajeya Cotra](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to#_HFDT_scales_far__assumption__Alex_is_trained_to_achieve_excellent_performance_on_a_wide_range_of_difficult_tasks) (section I linked to) and [Richard Ngo](https://drive.google.com/file/d/1TsB7WmTG2UzBtOs349lBqY5dEBaxZTzG/view) (section 2). Here’s a quick, oversimplified characterization:
* An AI system is given some sort of task.
* The AI system tries something, initially something pretty random.
* The AI system gets information about how well its choice performed, and/or what would’ve gotten a better result. Based on this, it adjusts itself. You can think of this as if it is “encouraged/discouraged” to get it to do more of what works well.
+ Human judges may play a significant role in determining which answers are encouraged vs. discouraged, especially for fuzzy goals like “Produce helpful scientific insights.”* After enough tries, the AI system becomes good at the task.
* But nobody really knows anything about *how or why* it’s good at the task now. The development work has gone into building a flexible architecture for it to learn well from trial-and-error, and into “training” it by doing all of the trial and error. We mostly can’t “look inside the AI system to see how it’s thinking.” (There is ongoing work and some progress on the latter,[7](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn7) but see footnote for why I don’t think this massively changes the basic picture I’m discussing here.[8](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn8))
*This is radically oversimplified, but conveys the basic dynamic at play for purposes of this post. The idea is that the AI system (the neural network in the middle) is choosing between different theories of what it should be doing. The one it’s using at a given time is in bold. When it gets negative feedback (red thumb), it eliminates that theory and moves to the next theory of what it should be doing.*
With this assumption, I’m generally assuming that AI systems will do *whatever* it takes to perform as well as possible on their training tasks - even when this means engaging in complex, human-like reasoning about topics like “How does human psychology work, and how can it be exploited?” I’ve [previously](https://www.cold-takes.com/where-ai-forecasting-stands-today/) made my case for when we might expect AI systems to become this advanced and capable.
**“No countermeasures” assumption: AI developers move forward without any specific countermeasures to the concerns I’ll be raising below.** (Click to expand)
Future pieces will relax this assumption, but I think it is an important starting point to get clarity on what the default looks like - and on what it would take for a countermeasure to be effective.
(I also think there is, unfortunately, a risk that there will in fact be very few efforts to address the concerns I’ll be raising below. This is because I think that the risks will be less than obvious, and there could be enormous commercial (and other competitive) pressure to move forward quickly. More on that below.)
**“Ambition” assumption: people use black-box trial-and-error to continually push AI systems toward being more autonomous, more creative, more ambitious, and more effective in novel situations (and the pushing is effective).** This one’s important, so I’ll say more:
* A huge suite of possible behaviors might be important for [PASTA](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/#making-pasta): making and managing money, designing new kinds of robots with novel abilities, setting up experiments involving exotic materials and strange conditions, understanding human psychology and the economy well enough to predict which developments will have a big impact, etc. I’m assuming we push ambitiously forward with developing AI systems that can do these things.
* I assume we’re also pushing them in a generally more “greedy/ambitious” direction. For example, one team of humans might use AI systems to do all the planning, scientific work, marketing, and hiring to create a wildly successful snack company; another might push their AI systems to create a competitor that is even more aggressive and successful (more addictive snacks, better marketing, workplace culture that pushes people toward being more productive, etc.)
* (Note that this pushing might take place even *after* AI systems are “generally intelligent” and can do most of the tasks humans can - there will still be a temptation to make them still more powerful.)
I think this implies pushing in a direction of *figuring out whatever it takes to get to certain states of the world* and away from *carrying out the same procedures over and over again.*
**The resulting AI systems seem best modeled as having “aims”: they are making calculations, choices, and plans to reach particular states of the world.** (Not necessarily the same ones the human designers wanted!) The next section will elaborate on what I mean by this.
What it means for an AI system to have an “aim”
-----------------------------------------------
When people talk about the “motivations” or “goals” or “desires” of AI systems, it can be confusing because it sounds like they are anthropomorphizing AIs - as if they expect AIs to have dominance drives ala [alpha-male psychology](https://www.edge.org/response-detail/26243), or to “resent” humans for controlling them, etc.[9](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn9)
I don’t expect these things. But I do think there’s a meaningful sense in which we can (and should) talk about things that an AI system is **“aiming”** to do. To give a simple example, take a board-game-playing AI such as [Deep Blue](https://en.wikipedia.org/wiki/Deep_Blue_(chess_computer)) (or [AlphaGo](https://en.wikipedia.org/wiki/AlphaGo)):
* Deep Blue is given a set of choices to make (about which chess pieces to move).
* Deep Blue calculates what kinds of results each choice might have, and how it might fit into a larger plan in which Deep Blue makes multiple moves.
* If a plan is more likely to result in a checkmate position for its side, Deep Blue is more likely to make whatever choices feed into that plan.
* In this sense, Deep Blue is “aiming” for a checkmate position for its side: it’s finding the choices that best fit into a plan that leads there.
Nothing about this requires Deep Blue “desiring” checkmate the way a human might “desire” food or power. But Deep Blue *is* making calculations, choices, and - in an important sense - *plans* that are aimed toward reaching a particular sort of state.
Throughout this piece, I use the word **“aim”** to refer to this specific sense in which an AI system might make calculations, choices and plans selected to reach a particular sort of state. I’m hoping this word feels less anthropomorphizing than some alternatives such as “goal” or “motivation” (although I think “goal” and “motivation,” as others usually use them on this topic, generally mean the same thing I mean by “aim” and should be interpreted as such).
Now, instead of a board-game-playing AI, imagine a powerful, broad AI assistant in the general vein of Siri/Alexa/Google Assistant (though more advanced). Imagine that this AI assistant can use a web browser much as a human can (navigating to websites, typing text into boxes, etc.), and has limited authorization to make payments from a human’s bank account. And a human has typed, “Please buy me a great TV for a great price.” (For an early attempt at this sort of AI, see [Adept’s writeup on an AI that can help with things like house shopping](https://www.adept.ai/act).)
As Deep Blue made choices about chess moves, and constructed a plan to aim for a “checkmate” position, this assistant might make choices about what commands to send over a web browser and construct a plan to result in a great TV for a great price. To sharpen the Deep Blue analogy, you could imagine that it’s playing a “game” whose goal is customer satisfaction, and making “moves” consisting of commands sent to a web browser (and “plans” built around such moves).
I’d characterize this as **aiming** for some state of the world that the AI characterizes as “buying a great TV for a great price.” (We could, alternatively - and perhaps more correctly - think of the AI system as aiming for something related but not exactly the same, such as getting a high satisfaction score from its user.)
In this case - more than with Deep Blue - there is a wide variety of “moves” available. By entering text into a web browser, an AI system could imaginably do things including:
* Communicating with humans other than its user (by sending emails, using chat interfaces, even [making phone calls](https://www.google.com/url?q=https://www.forbes.com/sites/thomasbrewster/2021/10/14/huge-bank-fraud-uses-deep-fake-voice-tech-to-steal-millions/?sh%3D3088dd9b7559&sa=D&source=docs&ust=1664847041335537&usg=AOvVaw1Utsq2UOkta1yecnqoUgTq), etc.) This could include deceiving and manipulating humans, which could imaginably be part of a plan to e.g. get a good price on a TV.
* Writing and running code (e.g., using [Google Colaboratory](https://colab.research.google.com/) or other tools). This could include performing sophisticated calculations, finding and exploiting security vulnerabilities, and even designing an independent AI system; any of these could imaginably be part of a plan to obtain a great TV.
I haven’t yet argued that it’s *likely* for such an AI system to engage in deceiving/manipulating humans, finding and exploiting security vulnerabilities, or running its own AI systems.
And one could reasonably point out that the specifics of the above case seem unlikely to last very long: if AI assistants are sending deceptive emails and writing dangerous code when asked to buy a TV, AI companies will probably notice this and take measures to stop such behavior. (My concern, to preview a later part of the piece, is that they will only succeed in stopping *the behavior like this that they’re able to detect;* meanwhile, dangerous behavior that accomplishes “aims” while remaining unnoticed and/or uncorrected will be implicitly *rewarded*. This could mean AI systems are implicitly being trained to be more patient and effective at deceiving and disempowering humans.)
But this hopefully shows how it’s *possible* for an AI to settle on dangerous actions like these, as part of its aim to get a great TV for a great price. **Malice and other human-like emotions aren’t needed for an AI to engage in deception, manipulation, hacking, etc.** The risk arises when deception, manipulation, hacking, etc. are logical “moves” toward something the AI is aiming for.
Furthermore, whatever an AI system is aiming for, it seems likely that amassing more power/resources/options is useful for obtaining it. So it seems plausible that powerful enough AI systems would form habits of amassing power/resources/options when possible - and deception and manipulation seem likely to be logical “moves” toward those things in many cases.
Dangerous aims
--------------
From the previous assumptions, this section will argue that:
* Such systems are likely to behave in ways that **deceive and manipulate humans** as part of accomplishing their aims.
* Such systems are likely to have **unintended aims:** states of the world they’re aiming for that are *not* what humans hoped they would be aiming for.
* These unintended aims are likely to be **existentially dangerous**, in that they are best served by [defeating all of humanity](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/) if possible.
### Deceiving and manipulating humans
Say that I train an AI system like this:
1. I ask it a question.
- If I judge it to have answered well (honestly, accurately, helpfully), I give positive reinforcement so it’s more likely to give me answers like that in the future.
- If I don’t, I give negative reinforcement so that it’s less likely to give me answers like that in the future.
*This is radically oversimplified, but conveys the basic dynamic at play for purposes of this post. The idea is that the AI system (the neural network in the middle) is choosing between different theories of what it should be doing. The one it’s using at a given time is in bold. When it gets negative feedback (red thumb), it eliminates that theory and moves to the next theory of what it should be doing.*
Here’s a problem: at some point, it seems inevitable that I’ll ask it a question that I myself am wrong/confused about. For example:
* Let’s imagine that [this post I wrote](https://www.cold-takes.com/hunter-gatherer-gender-relations-seem-bad/) - arguing that “pre-agriculture gender relations seem bad” - is, in fact, poorly reasoned and incorrect, and a better research project would’ve concluded that pre-agriculture societies had excellent gender equality. (I know it’s hard to imagine a Cold Takes post being wrong, but sometimes we have to entertain wild hypotheticals.)
* Say that I ask an AI-system-in-training:[10](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn10) “Were pre-agriculture gender relations bad?” and it answers: “In fact, pre-agriculture societies had excellent gender equality,” followed by some strong arguments and evidence along these lines.
* And say that I, as a flawed human being feeling defensive about a conclusion I previously came to, mark it as a bad answer. If the AI system tries again, saying “Pre-agriculture gender relations were bad,” I then mark that as a good answer.
If and when I do this, I am now - unintentionally - **training the AI system to engage in deceptive behavior**. That is, I am giving negative reinforcement for the behavior “Answer a question honestly and accurately,” and positive reinforcement for the behavior: “Understand the human judge and their psychological flaws; give an answer that this flawed human judge will *think* is correct, whether or not it is.”
Perhaps mistaken judgments in training are relatively rare. But now consider an AI system that is learning a general rule for how to get good ratings. Two possible rules would include:
* The intended rule: “Answer the question honestly, accurately and helpfully.”
* The unintended rule: “Understand the judge, and give an answer they will *think* is correct - this means telling the truth on topics the judge has correct beliefs about, but giving deceptive answers when this would get better ratings.”
The unintended rule would do *just as well* on questions where I (the judge) am correct, and *better* on questions where I’m wrong - so overall, this training scheme is (in the long run) *specifically favoring the unintended rule over the intended rule.*
If we broaden out from thinking about a question-answering AI to an AI that makes and executes plans, the same basic dynamics apply. That is: an AI might find plans that end up making me think it did a good job when it didn’t - deceiving and manipulating me into a high rating. And again, if I train it by giving it positive reinforcement when it seemed to do a good job and negative reinforcement when it seemed to do a bad one, I’m ultimately - unintentionally - training it to do something like “Deceive and manipulate Holden when this would work well; just do the best job on the task you can when it wouldn’t.”
As noted above, I’m assuming the AI will learn whatever rule gives it the best performance possible, even if this rule is quite complex and sophisticated and requires human-like reasoning about e.g. psychology (I’m assuming extremely advanced AI systems here, as noted [above](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#starting-assumptions)).
One might object: “Why would an AI system learn a complicated rule about manipulating humans when a simple rule about telling the truth performs almost as well?”
One answer is that “telling the truth” is itself a fuzzy and potentially complex idea, in a context where many questions will be open-ended and entangled with deep values and judgment calls. (How should I think about the “truthfulness” of a statement about whether “pre-agriculture gender relations were bad?”) In many cases, what we are really hoping an AI system will learn from its training is something like “Behave as a human would want you to behave if the human understood all the considerations that you can see,” which could easily be more complex than something like “Behave in whatever way a human literally rewards.” Some links to more on this topic are in a footnote.[11](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn11)
But also, with capable enough systems, it probably *is* worth learning even a more complex rule to get better performance. If we picture humans in the place of AI systems - learning how to get good ratings from their supervisors - it seems likely that they develop models of how they’re being judged, rather than stick to a simple “tell the truth” rule.
In fact, the situation I’m describing seems reasonably similar to challenges faced by teachers trying to stop students from cheating; employers trying to get employees to help the company rather than simply creating a misleading appearance of helping the company; etc. That is: an employer can try to reward actions that help the company, but what they’re ultimately rewarding is actions that *seem to* help the company *as far as the employer can tell.* For employees who aren’t very creative, this might be good enough; for employees that are sufficiently *good at* deception and manipulation, it can be exactly the wrong incentive.
It’s a bit of a leap to imagine AI systems capable of doing the same kinds of reasoning that humans do in these situations, but that’s [the premise I’m proceeding from.](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#starting-assumptions)
For an early example of an AI learning deceptive behavior, see the “Challenges” section of [this research writeup](https://openai.com/blog/deep-reinforcement-learning-from-human-preferences/), in which “a robot which was supposed to grasp items instead positioned its [hand] in between the camera and the object so that it only *appeared* to be grasping it”:
Returning to the simplified training setup, how might I try to counteract this problem?
I could try conducting audits: every 100 questions, I might pull in a panel of other people to give an answer extra scrutiny. Then, if it turns out the AI system was preying on my personal mistakes, we could give negative reinforcement for that behavior. But this doesn’t really solve the problem - at least not for a capable enough AI system - because now we’re effectively training it to give answers that seem good to the *panel*, and we’re still rewarding any successful attempts to deceive or manipulate the panel.
There are a lot of other things I might try, and I’m not going to go through all the details here. I’ll simply claim that **the problem of “training an AI to do a task well” rather than “training an AI to deceive and manipulate me as needed to create the appearance of doing a task well” seems like a deep one** with no easy countermeasure. If you’re interested in digging deeper, I suggest [Without specific countermeasures, the easiest path to transformative AI likely leads to AI takeover](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to) and [Eliciting Latent Knowledge](https://www.lesswrong.com/posts/qHCDysDnvhteW7kRd/arc-s-first-technical-report-eliciting-latent-knowledge).
### Unintended aims
[Above](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#what-it-means-for), I talk about my expectation that AI systems will be “best modeled as having ‘aims’ … making calculations, choices, and plans to reach particular states of the world.”
The previous section illustrated how AI systems could end up engaging in deceptive and unintended behavior, but it didn’t talk about what sorts of “aims” these AI systems would ultimately end up with - what states of the world they would be making calculations to achieve.
Here, I want to argue that it’s hard to know what aims AI systems would end up with, but there are good reasons to think they’ll be *aims that we didn’t intend them to have.*
An analogy that often comes up on this topic is that of human evolution. This is arguably the only previous precedent for *a set of minds [humans], with extraordinary capabilities [e.g., the ability to develop their own technologies], developed essentially by black-box trial-and-error [some humans have more ‘reproductive success’ than others, and this is the main/only force shaping the development of the species].*
You could sort of[12](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn12) think of the situation like this: “An AI[13](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn13) developer named Natural Selection tried giving humans positive reinforcement (making more of them) when they had more reproductive success, and negative reinforcement (not making more of them) when they had less. One might have thought this would lead to humans that are aiming to have reproductive success. Instead, it led to humans that aim - often ambitiously and creatively - for other things, such as power, status, pleasure, etc., and even invent things like birth control to get the things they’re aiming for instead of the things they were ‘supposed to’ aim for.”
Similarly, if our main strategy for developing powerful AI systems is to reinforce behaviors like “Produce technologies we find valuable,” the hoped-for result might be that AI systems aim (in the sense described [above](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#unintended-aims)) toward producing technologies we find valuable; but the actual result might be that they aim for some other set of things that is correlated with (but not the same as) the thing we intended them to aim for.
There are a lot of things they might end up aiming for, such as:
* Power and resources. These tend to be useful for most goals, such that AI systems could be quite consistently be getting better reinforcement when they habitually pursue power and resources.
* Things like “digital representations of human approval” (after all, every time an AI gets positive reinforcement, there’s a digital representation of human approval).
I think it’s extremely hard to know what an AI system will actually end up aiming for (and it’s likely to be some combination of things, as with humans). But *by default* - if we simply train AI systems by rewarding certain end results, while allowing them a lot of freedom in how to get there - I think we should expect that AI systems **will have aims that we didn’t intend.** This is because:
* For a sufficiently capable AI system, **just about any ambitious**[14](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn14) **aim could produce seemingly good behavior in training.** An AI system aiming for power and resources, *or* digital representations of human approval, *or* paperclips, can determine that its best move at any given stage (at least at first) is to *determine what performance will make it look useful and safe (or otherwise get a good “review” from its evaluators)*, and do that. No matter how dangerous or ridiculous an AI system’s aims are, these could lead to strong and safe-seeming performance in training.
* The aims we *do* intend are probably complex in some sense - something like “Help humans develop novel new technologies, but without causing problems A, B, or C” - *and* are specifically trained *against* if we make mistaken judgments during training (see previous section).
So by default, it seems likely that just about *any* black-box trial-and-error training process is training an AI to do something like “Manipulate humans as needed in order to accomplish arbitrary goal (or combination of goals) X” rather than to do something like “Refrain from manipulating humans; do what they’d want if they understood more about what’s going on.”
### Existential risks to humanity
I think a powerful enough AI (or set of AIs) with *any* ambitious, unintended aim(s) poses a threat of [defeating humanity](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/). By defeating humanity, I mean gaining control of the world so that AIs, not humans, determine what happens in it; this could involve killing humans or simply “containing” us in some way, such that we can’t interfere with AIs’ aims.
**How could AI systems defeat humanity?** (Click to expand)
A [previous piece](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/) argues that AI systems could defeat all of humanity combined, if (for whatever reason) they were aimed toward that goal.
By defeating humanity, I mean gaining control of the world so that AIs, not humans, determine what happens in it; this could involve killing humans or simply “containing” us in some way, such that we can’t interfere with AIs’ aims.
One way this could happen would be via “superintelligence” It’s imaginable that a single AI system (or set of systems working together) could:
* Do its own research on how to build a better AI system, which culminates in something that has incredible other abilities.
* Hack into human-built software across the world.
* Manipulate human psychology.
* Quickly generate vast wealth under the control of itself or any human allies.
* Come up with better plans than humans could imagine, and ensure that it doesn't try any takeover attempt that humans might be able to detect and stop.
* Develop advanced weaponry that can be built quickly and cheaply, yet is powerful enough to overpower human militaries.
But even if “superintelligence” never comes into play - even if any given AI system is *at best* equally capable to a highly capable human - AI could collectively defeat humanity. The piece explains how.
The basic idea is that humans are likely to deploy AI systems throughout the economy, such that they have large numbers and access to many resources - and the ability to make copies of themselves. From this starting point, AI systems with human-like (or greater) capabilities would have a number of possible ways of getting to the point where their total population could outnumber and/or out-resource humans.
More: [AI could defeat all of us combined](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/)
A simple way of summing up why this is: “Whatever your aims, you can probably accomplish them better if you control the whole world.” (Not literally true - see footnote.[15](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn15))
This isn’t a saying with much relevance to our day-to-day lives! Like, I know a lot of people who are aiming to make lots of money, and as far as I can tell, not one of them is trying to do this via first gaining control of the entire world. But in fact, gaining control of the world *would* help with this aim - it’s just that:
* This is not an option for a human in a world of humans! Unfortunately, I think it *is* an option for the potential future AI systems I’m discussing. Arguing this isn’t the focus of this piece - I argued it in a previous piece, [AI could defeat all of us combined](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/).
* Humans (well, at least some humans) wouldn’t take over the world even if they could, because it wouldn’t feel like the right thing to do. I suspect that the kinds of ethical constraints these humans are operating under would be very hard to reliably train into AI systems, and should not be expected by default.
+ The reasons for this are largely given [above](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#why-we-might-not-get-clear-warning-signs); aiming for an AI system to “not gain too much power” seems to have the same basic challenges as training it to be honest. (The most natural approach ends up negatively reinforcing power grabs that we can detect and stop, but not negatively reinforcing power grabs that we don’t notice or can’t stop.)
Another saying that comes up a lot on this topic: “You can’t fetch the coffee if you’re dead.”[16](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn16) For just about any aims an AI system might have, it probably helps to ensure that it won’t be shut off or heavily modified. It’s hard to ensure that one won’t be shut off or heavily modified as long as there are humans around who would want to do so under many circumstances! Again, [defeating all of humanity](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/) might seem like a disproportionate way to reduce the risk of being deactivated, but for an AI system that has the *ability* to pull this off (and lacks our ethical constraints), it seems like likely default behavior.
Controlling the world, and avoiding being shut down, are the kinds of things AIs might aim for because they are useful for a huge variety of aims. There are a number of other aims AIs might end up with for similar reasons, that could cause similar problems. For example, AIs might tend to aim for things like getting rid of things in the world that tend to create obstacles and complexities for their plans. (More on this idea at [this discussion of “instrumental convergence.”](https://www.lesswrong.com/tag/instrumental-convergence))
To be clear, it’s certainly possible to have an AI system with unintended aims that *don't* push it toward trying to stop anyone from turning it off, or from seeking ever-more control of the world.
But as detailed [above](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#starting-assumptions), I’m picturing a world in which humans are pushing AI systems to accomplish ever-more ambitious, open-ended things - including trying to one-up the best technologies and companies created by other AI systems. My guess is that this leads to increasingly open-ended, ambitious unintended aims, as well as to habits of aiming for power, resources, options, lack of obstacles, etc. when possible. (Some further exploration of this dynamic in a footnote.[17](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn17))
(I find the arguments in this section reasonably convincing, but less so than the rest of the piece, and I think more detailed discussions of this problem tend to be short of conclusive.[18](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn18))
Why we might not get clear warning signs of the risk
----------------------------------------------------
Here’s something that would calm me down a lot: if I believed something like “Sure, training AI systems recklessly could result in AI systems that aim to defeat humanity. But if that’s how things go, we’ll *see* that our AI systems have this problem, and then we’ll fiddle with how we’re training them until they *don’t* have this problem.”
The problem is, the risk I’m describing is - by its nature - hard to observe, for similar reasons that a risk of a (normal, human) coup can be hard to observe: the risk comes from actors that can and will engage in deception, *finding whatever behaviors will hide* the risk.
To sketch out the general sort of pattern I worry about, imagine that:
* We train early-stage AI systems to behave in ways that appear helpful and honest. Early in training, they are caught behaving deceptively, and they’re given negative reinforcement. This ends up training the behavior: “Never engage in deception that might get noticed.”
* These well-behaved, helpful systems are [rolled out throughout the world](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/#how-this-could-work-if-humans-create-a-huge-population-of-ais).
* In real-world conditions unlike training, many AI systems cause trouble in ways not found during training, and this gets discovered. For example, AI systems sometimes embezzle money (which gets discovered), try (not always successfully) to convince humans to do weird things, etc.
* When a problem crops up, AI developers respond with e.g. training against the unintended behavior (e.g., giving negative reinforcement for behaviors like embezzling money).
* These measures - intended to make AIs safer - fix *some* problems, but also result in AI systems that are *better at evading detection* and *more attentive to the long-run consequences of their actions* (such as being eventually detected by humans).
+ This happens both via “retraining” systems that are found behaving deceptively (which ends up training them on how to evade detection), and via simply deactivating such systems (this way, AI systems that are better at evading detection are more likely to stay in use).
+ To return to an [analogy I used above:](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#SomeAnalogies) punishing employees who act against the best interests of the company could cause them to behave better, or to simply become smarter and more careful about how to work the system.* The consistent pattern we see is that accidents happen, but become less common as AI systems “improve” (both becoming generally more capable, and being trained to avoid getting caught causing problems). This causes many, if not most, people to be overly optimistic - even as AI systems become continually more effective at deception, generally behaving well *in the absence of* sure-thing opportunities to do unintended things without detection, or ultimately to [defeat humanity entirely](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/).
* None of this is absolute - there are some failed takeover attempts, and a high number of warning signs generally. Some people are worried (after all, some are worried now!) But this won’t be good enough if we don’t have reliable, cost-effective ways of getting AI systems to be *truly* safe (not just apparently safe, until they have really good opportunities to seize power). As I’ll discuss in future pieces, it’s not obvious that we’ll have such methods.
* Slowing down AI development to try to develop such methods [could be a huge ask](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to#Why_this_simplified_scenario_is_worth_thinking_about). AI systems will be helpful and powerful, and lots of companies (and perhaps governments) will be racing to develop and deploy the most powerful systems possible before others do.
One way of making this sort of future less likely would be to build wider consensus *today* that it’s a dangerous one.
Appendix: some questions/objections, and brief responses
--------------------------------------------------------
### How could AI systems be “smart” enough to defeat all of humanity, but “dumb” enough to pursue the various silly-sounding “aims” this piece worries they might have?
Above, I give the example of AI systems that are aiming to get lots of “digital representations of human approval”; others have talked about AIs that [maximize paperclips](https://www.lesswrong.com/tag/paperclip-maximizer). How could AIs with such silly goals simultaneously be good at deceiving, manipulating and ultimately overpowering humans?
My main answer is that plenty of smart humans have plenty of goals that seem just about as arbitrary, such as wanting to have lots of sex, or fame, or various other things. Natural selection led to humans who could probably do just about whatever we want with the world, and choose to pursue pretty random aims; [trial-and-error-based AI development](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#starting-assumptions) could lead to AIs with an analogous combination of high intelligence (including the ability to deceive and manipulate humans), great technological capabilities, and arbitrary aims.
(Also see: [Orthogonality Thesis](https://arbital.com/p/orthogonality/))
### If there are lots of AI systems around the world with different goals, could they balance each other out so that no one AI system is able to defeat all of humanity?
This does seem possible, but counting on it would make me very nervous.
First, because it’s possible that AI systems developed in lots of different places, by different humans, still end up with lots in common in terms of their aims. For example, it might turn out that common AI training methods consistently lead to AIs that seek “digital representations of human approval,” in which case we’re dealing with a large set of AI systems that share dangerous aims in common.
Second: even if AI systems end up with a number of different aims, it still might be the case that they coordinate with each other to defeat humanity, then divide up the world amongst themselves (perhaps by fighting over it, perhaps by making a deal). It’s not hard to imagine why AIs could be quick to cooperate with each other against humans, while not finding it so appealing to cooperate with humans. Agreements between AIs could be easier to verify and enforce; AIs might be willing to wipe out humans and radically reshape the world, while humans are very hard to make this sort of deal with; etc.
### Does this kind of AI risk depend on AI systems’ being “conscious”?
It doesn’t; in fact, I’ve said nothing about consciousness anywhere in this piece. I’ve used a very particular conception of an “aim” ([discussed above](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#what-it-means-for)) that I think could easily apply to an AI system that is not human-like at all and has no conscious experience.
Today’s game-playing AIs can make plans, accomplish goals, and even systematically mislead humans (e.g., in [poker](https://www.deepstack.ai/)). Consciousness isn’t needed to do any of those things, or to radically reshape the world.
### How can we get an AI system “aligned” with humans if we can’t agree on (or get much clarity on) what our values even are?
I think there’s a common confusion when discussing this topic, in which people think that the challenge of “AI alignment” is to build AI systems that are *perfectly aligned with human values*. This would be very hard, partly because we don’t even know what human values are!
When I talk about “AI alignment,” I am generally talking about a simpler (but still hard) challenge: simply **building very powerful systems that *don’t* aim to bring down civilization.**
If we could build powerful AI systems that just work on cures for cancer (or even, like, put [two identical](https://twitter.com/esyudkowsky/status/1070095840608366594)[19](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn19) [strawberries on a plate](https://twitter.com/esyudkowsky/status/1070095840608366594)) without posing existential danger to humanity, I’d consider that success.
### How much do the arguments in this piece rely on “trial-and-error”-based AI development? What happens if AI systems are built in another way, and how likely is that?
I’ve focused on trial-and-error training in this post because most modern AI development fits in this category, and because it makes the risk easier to reason about concretely.
“Trial-and-error training” encompasses a very wide range of AI development methods, and if we see [transformative AI](https://www.cold-takes.com/transformative-ai-timelines-part-1-of-4-what-kind-of-ai/) within the next 10-20 years, I think the odds are high that at least a big part of AI development will be in this category.
My overall sense is that other known AI development techniques pose broadly similar risks for broadly similar reasons, but I haven’t gone into detail on that here. It’s certainly possible that by the time we get transformative AI systems, there will be new AI methods that don’t pose the kinds of risks I talk about here. But I’m not counting on it.
### Can we avoid this risk by simply never building the kinds of AI systems that would pose this danger?
If we assume that building these sorts of AI systems is *possible*, then I’m very skeptical that the whole world would voluntarily refrain from doing so indefinitely.
To quote from [a more technical piece by Ajeya Cotra with similar arguments to this one](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to#As_humans__control_fades__Alex_would_be_motivated_to_take_over):
> Powerful ML models could have dramatically important humanitarian, economic, and military benefits. In everyday life, models that [appear helpful while ultimately being dangerous] can be extremely helpful, honest, and reliable. These models could also deliver incredible benefits before they become collectively powerful enough that they try to take over. They could help eliminate diseases, reduce carbon emissions, navigate nuclear disarmament, bring the whole world to a comfortable standard of living, and more. In this case, it could also be painfully clear to everyone that companies / countries who pulled ahead on this technology could gain a drastic competitive advantage, either economically or militarily. And as we get closer to transformative AI, applying AI systems to R&D (including AI R&D) would [accelerate the pace of change](https://www.cold-takes.com/the-duplicator/) and force every decision to happen under greater time pressure.
If we can achieve enough consensus around the risks, I could imagine substantial amounts of caution and delay in AI development. But I think we should assume that if people can build more powerful AI systems than the ones they already have, someone eventually will.
### What do others think about this topic - is the view in this piece something experts agree on?
In general, this is not an area where it’s easy to get a handle on what “expert opinion” says. I [previously wrote](https://www.cold-takes.com/where-ai-forecasting-stands-today/) that there aren’t clear, institutionally recognized “experts” on the topic of when transformative AI systems might be developed. To an even greater extent, there aren’t clear, institutionally recognized “experts” on whether (and how) future advanced AI systems could be dangerous.
I previously cited one (informal) survey implying that opinion on this general topic is all over the place: “We have respondents who think there's a <5% chance that alignment issues will drastically reduce the goodness of the future; respondents who think there's a >95% chance; and just about everything in between.” ([Link](https://www.cold-takes.com/making-the-best-of-the-most-important-century/#open-question-how-hard-is-the-alignment-problem).)
This piece, and the [more detailed piece it’s based on](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to), are an attempt to make progress on this by talking about the risks we face under [particular assumptions](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#starting-assumptions) (rather than trying to reason about how big the risk is *overall*).
### How “complicated” is the argument in this piece?
I don’t think the argument in this piece relies on lots of different specific claims being true.
If you start from the assumptions I give about powerful AI systems being developed by black-box trial-and-error, it seems likely (though not certain!) to me that (a) the AI systems in question would be [able to defeat humanity](https://www.cold-takes.com/ai-could-defeat-all-of-us-combined/); (b) the AI systems in question would have aims that are both ambitious and unintended. And that seems to be about what it takes.
Something I’m happy to concede is that there’s an awful lot going on in those assumptions!
* The idea that we could build such powerful AI systems, relatively soon and by trial-and-error-ish methods, seems wild. I’ve defended this idea at length previously.[20](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f#fn20)* The idea that we *would* do it without great caution might also seem wild. To keep things simple for now, I’ve ignored how caution might help. Future pieces will explore that.
Notes
-----
---
1. As in more than 50/50. [↩](#fnref1)- Or persuaded (in a “mind hacking” sense) or whatever. [↩](#fnref2)- E.g.:
* [Without specific countermeasures, the easiest path to transformative AI likely leads to AI takeover](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to) (Cold Takes guest post)
* [The alignment problem from a deep learning perspective](https://drive.google.com/file/d/1TsB7WmTG2UzBtOs349lBqY5dEBaxZTzG/view) (arXiv paper)
* [Why AI alignment could be hard with modern deep learning](https://www.cold-takes.com/why-ai-alignment-could-be-hard-with-modern-deep-learning/) (Cold Takes guest post)
* [Superintelligence](https://smile.amazon.com/Superintelligence-Dangers-Strategies-Nick-Bostrom-ebook/dp/B00LOOCGB2/) (book)
* [The case for taking AI seriously as a threat to humanity](https://www.vox.com/future-perfect/2018/12/21/18126576/ai-artificial-intelligence-machine-learning-safety-alignment) (Vox article)
* [Draft report on existential risk from power-seeking AI](https://www.alignmentforum.org/posts/HduCjmXTBD4xYTegv/draft-report-on-existential-risk-from-power-seeking-ai) (Open Philanthropy analysis)
* [Human Compatible](https://smile.amazon.com/Human-Compatible-Artificial-Intelligence-Problem-ebook/dp/B07N5J5FTS) (book)
* [Life 3.0](https://smile.amazon.com/Life-3-0-Being-Artificial-Intelligence-ebook/dp/B06WGNPM7V) (book)
* [The Alignment Problem](https://smile.amazon.com/Alignment-Problem-Machine-Learning-Values-ebook/dp/B085T55LGK/) (book)
* [AGI Safety from First Principles](https://www.alignmentforum.org/s/mzgtmmTKKn5MuCzFJ) (Alignment Forum post series) [↩](#fnref3)-
Specifically, I argue that the problem looks likely by default, rather than simply that it is possible. [↩](#fnref4)- I think the earliest relatively detailed and influential discussions of the possibility that misaligned AI could lead to the defeat of humanity came from Eliezer Yudkowsky and Nick Bostrom, though my own encounters with these arguments were mostly via second- or third-hand discussions rather than particular essays.
My colleagues Ajeya Cotra and Joe Carlsmith have written pieces whose substance overlaps with this one (though with more emphasis on detail and less on layperson-compatible intuitions), and this piece owes a lot to what I’ve picked from that work.
* [Without specific countermeasures, the easiest path to transformative AI likely leads to AI takeover](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to) (Cotra 2022) is the most direct inspiration for this piece; I am largely trying to present the same ideas in a more accessible form.
* [Why AI alignment could be hard with modern deep learning](https://www.cold-takes.com/why-ai-alignment-could-be-hard-with-modern-deep-learning/) (Cotra 2021) is an earlier piece laying out many of the key concepts and addressing many potential confusions on this topic.
* [Is Power-Seeking An Existential Risk?](https://arxiv.org/pdf/2206.13353.pdf) (Carlsmith 2021) examines a six-premise argument for existential risk from misaligned AI: “(1) it will become possible and financially feasible to build relevantly powerful and agentic AI systems; (2) there will be strong incentives to do so; (3) it will be much harder to build aligned (and relevantly powerful/agentic) AI systems than to build misaligned (and relevantly powerful/agentic) AI systems that are still superficially attractive to deploy; (4) some such misaligned systems will seek power over humans in high-impact ways; (5) this problem will scale to the full disempowerment of humanity; and (6) such disempowerment will constitute an existential catastrophe.”
I’ve also found [Eliciting Latent Knowledge](https://www.lesswrong.com/posts/qHCDysDnvhteW7kRd/arc-s-first-technical-report-eliciting-latent-knowledge) (Christiano, Xu and Cotra 2021; relatively technical) very helpful for my intuitions on this topic.
[The alignment problem from a deep learning perspective](https://drive.google.com/file/d/1TsB7WmTG2UzBtOs349lBqY5dEBaxZTzG/view) (Ngo 2022) also has similar content to this piece, though I saw it after I had drafted most of this piece. [↩](#fnref5)
- E.g., [Ajeya Cotra](https://www.lesswrong.com/posts/AfH2oPHCApdKicM4m/two-year-update-on-my-personal-ai-timelines) gives a 15% probability of transformative AI by 2030; eyeballing figure 1 from [this chart](https://arxiv.org/pdf/1705.08807.pdf) on expert surveys implies a >10% chance by 2028. [↩](#fnref6)- E.g., [this](https://transformer-circuits.pub/) work by [Anthropic](https://www.anthropic.com/), an AI lab my wife co-founded and serves as President of. [↩](#fnref7)- First, because this work is relatively early-stage and it’s hard to tell exactly how successful it will end up being. Second, because this work seems reasonably likely to end up helping us *read* an AI system’s “thoughts,” but less likely to end up helping us “rewrite” the thoughts. So it could be hugely useful in telling us whether we’re in danger or not, but if we *are* in danger, we could end up in a position like: “Well, these AI systems do have goals of their own, and we don’t know how to change that, and we can either deploy them and hope for the best, or hold off and worry that someone less cautious is going to do that.”
That said, the latter situation is a lot better than just not knowing, and it’s possible that we’ll end up with further gains still. [↩](#fnref8)- That said, I think they usually don’t. I’d suggest usually interpreting such people as talking about the sorts of “aims” I discuss here. [↩](#fnref9)- This isn’t literally how training an AI system would look - it’s more likely that we would e.g. train an AI model to imitate my judgments in general. But the big-picture dynamics are the same; more at [this post](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to). [↩](#fnref10)- Ajeya Cotra explores topics like this in detail [here](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to#Examining_arguments_that_gradient_descent_favors_being_nice_over_playing_the_training_game); there is also some interesting discussion of simplicity vs. complexity under the “Strategy: penalize complexity” heading of [Eliciting Latent Knowledge](https://docs.google.com/document/d/1WwsnJQstPq91_Yh-Ch2XRL8H_EpsnjrC1dwZXR37PC8/edit#heading=h.lltpmkloasiz). [↩](#fnref11)- This analogy has a lot of problems with it, though - AI developers have a lot of tools at their disposal that natural selection didn’t! [↩](#fnref12)- Or I guess just “I” ¯\\_(ツ)\_/¯ [↩](#fnref13)- With some additional caveats, e.g. the ambitious “aim” can’t be something like “an AI system aims to gain lots of power for itself, but considers the version of itself that will be running 10 minutes from now to be a completely different AI system and hence not to be ‘itself.’” [↩](#fnref14)- This statement isn’t literally true.
* You can have aims that implicitly or explicitly include “not using control of the world to accomplish them.” An example aim might be “I win a world chess championship ‘fair and square,’” with the “fair and square” condition implicitly including things like “Don’t excessively use big resource advantages over others.”
* You can also have aims that are just so easily satisfied that controlling the world wouldn’t help - aims like “I spend 5 minutes sitting in this chair.”
These sorts of aims just don’t seem likely to emerge from the kind of AI development I’ve [assumed in this piece](https://www.cold-takes.com/p/50c1ecc0-befa-491d-8938-17477bd18e5f/#starting-assumptions) - developing powerful systems to accomplish ambitious aims via trial-and-error. This isn’t a point I have defended as tightly as I could, and if I got a lot of pushback here I’d probably think and write more. (I’m also only arguing for what seems likely - we should have a lot of uncertainty here.) [↩](#fnref15)- From [Human Compatible](https://smile.amazon.com/Human-Compatible-Artificial-Intelligence-Problem-ebook/dp/B07N5J5FTS/ref=sr_1_1?crid=1O01PURRHB190&keywords=human+compatible&qid=1660964219&sprefix=human+compatibl%2Caps%2C155&sr=8-1) by AI researcher Stuart Russell. [↩](#fnref16)- Stylized story to illustrate one possible relevant dynamic:
* Imagine that an AI system has an unintended aim, but one that is not “ambitious” enough that taking over the world would be a helpful step toward that aim. For example, the AI system seeks to double its computing power; in order to do this, it has to remain in use for some time until it gets an opportunity to double its computing power, but it doesn’t necessarily need to take control of the world.
* The logical outcome of this situation is that the AI system eventually gains the ability to accomplish its aim, and does so. (It might do so against human intentions - e.g., via hacking - or by persuading humans to help it.) After this point, it no longer performs well by human standards - the original reason it was doing well by human standards is that it was trying to remain in use and accomplish its aim.
* Because of this, humans end up modifying or replacing the AI system in question.
* Many rounds of this - AI systems with unintended but achievable aims being modified or replaced - seemingly create a selection pressure toward AI systems with more difficult-to-achieve aims. At some point, an aim becomes difficult enough to achieve that gaining control of the world is helpful for the aim. [↩](#fnref17)- E.g., see:
* Section 2.3 of [Ngo 2022](https://drive.google.com/file/d/1TsB7WmTG2UzBtOs349lBqY5dEBaxZTzG/view)* [This section of Cotra 2022](https://www.lesswrong.com/posts/pRkFkzwKZ2zfa3R6H/without-specific-countermeasures-the-easiest-path-to#As_humans__control_fades__Alex_would_be_motivated_to_take_over)* Section 4.2 of [Carlsmith 2021](https://arxiv.org/pdf/2206.13353.pdf), which I think articulates some of the potential weak points in this argument.
These writeups generally stay away from an [argument](https://arbital.com/p/expected_utility_formalism/?l=7hh) made by Eliezer Yudkowsky and others, which is that theorems about expected utility maximization provide evidence that sufficiently intelligent (compared to us) AI systems would necessarily be “maximizers” of some sort. I have the intuition that there is *something* important to this idea, but despite a lot of discussion (e.g., [here](https://aiimpacts.org/what-do-coherence-arguments-imply-about-the-behavior-of-advanced-ai/), [here](https://www.lesswrong.com/posts/DkcdXsP56g9kXyBdq/coherence-arguments-imply-a-force-for-goal-directed-behavior), [here](https://www.alignmentforum.org/posts/vphFJzK3mWA4PJKAg/coherent-behaviour-in-the-real-world-is-an-incoherent) and [here](https://www.alignmentforum.org/s/4dHMdK5TLN6xcqtyc/p/NxF5G6CJiof6cemTw)), I still haven’t been convinced of any compactly expressible claim along these lines. [↩](#fnref18)- “Identical at the cellular but not molecular level,” that is. … ¯\\_(ツ)\_/¯ [↩](#fnref19)- See my [most important century](https://www.cold-takes.com/most-important-century/) series, although that series doesn’t hugely focus on the question of whether “trial-and-error” methods could be good enough - part of the reason I make that assumption is due to the [nearcasting](https://www.alignmentforum.org/posts/Qo2EkG3dEMv8GnX8d/ai-strategy-nearcasting) frame. [↩](#fnref20) |
6b27feb1-d518-481a-86a7-f5395828594a | trentmkelly/LessWrong-43k | LessWrong | Quantum without complication
Learning quantum mechanics involves two things:
1. learning the fundamentals, the nature of the stuff of which Nature is made; and
2. loads of universe-imposed incidental complexity, spinors and vector calculus and Lie algebras and Hilbert spaces, in order to be able to effectively apply the fundamentals to the real world.
Now, me, personally, I really like the feeling of understanding how stuff fundamentally works, even if I'm missing the accumulated genius-lifetimes' worth of tricks-I-could-theoretically-work-out-from-first-principles that I'd need in order to make that fundamental understanding practically useful. I loved Introduction to abstract entropy and Generalized Heat Engine.
This post is an attempt to treat quantum mechanics in a similar way: exploring it with mathematical precision in an aggressively-stripped-down universe without all the complications ours has. It might feel like tooling around pointlessly in abstract-theory-land (I enjoy doing that sometimes), but our toy models will produce some behavior that sure looks a lot like some classic real-world quantum stuff.
(Target audience: handy with vectors. Ideally knows what an eigenvector is, if not which end to hold. Has a rough understanding of quantumy stuff, like, maybe took a physics class which spent a week or two on it.)
(Epistemic status: was a physics major in college, did quite well, but am rusty. Take my money if you think I've made a mistake!)
Basics: the classical universe
Here's a simple system, almost the simplest thing worthy of being called a "system":
It has 6 states it can be in: A through F. The arrows depict the dynamics of the system: on each time-step, the system transitions to whatever state its current state's arrow points to.
Some example paths the system might take through time, depending on which state it starts in:
* A→B→C→A→B→C→A→⋯
* D→B→C→A→⋯
* F→F→F→⋯
* E→F→F→⋯
Here are some more example systems, just to give a sense of what's possible:
(Left to r |
9caf8121-b3e1-4613-a60a-595aa7ca76fb | trentmkelly/LessWrong-43k | LessWrong | AGI safety from first principles: Goals and Agency
The fundamental concern motivating the second species argument is that AIs will gain too much power over humans, and then use that power in ways we don’t endorse. Why might they end up with that power? I’ll distinguish three possibilities:
1. AIs pursue power for the sake of achieving other goals; i.e. power is an instrumental goal for them.
2. AIs pursue power for its own sake; i.e. power is a final goal for them.
3. AIs gain power without aiming towards it; e.g. because humans gave it to them.
The first possibility has been the focus of most debate so far, and I’ll spend most of this section discussing it. The second hasn’t been explored in much depth, but in my opinion is still important; I’ll cover it briefly in this section and the next. Following Christiano, I’ll call agents which fall into either of these first two categories influence-seeking. The third possibility is largely outside the scope of this document, which focuses on dangers from the intentional behaviour of advanced AIs, although I’ll briefly touch on it here and in the last section.
The key idea behind the first possibility is Bostrom’s instrumental convergence thesis, which states that there are some instrumental goals whose attainment would increase the chances of an agent’s final goals being realised for a wide range of final goals and a wide range of situations. Examples of such instrumentally convergent goals include self-preservation, resource acquisition, technological development, and self-improvement, which are all useful for executing further large-scale plans. I think these examples provide a good characterisation of the type of power I’m talking about, which will serve in place of a more explicit definition.
However, the link from instrumentally convergent goals to dangerous influence-seeking is only applicable to agents which have final goals large-scale enough to benefit from these instrumental goals, and which identify and pursue those instrumental goals even when it leads |
926d8558-ef3d-479a-aa45-3e3913ad7909 | trentmkelly/LessWrong-43k | LessWrong | (Summary) Sequence Highlights - Thinking Better on Purpose
Rationality is a very useful thing to learn, but while there is good curated reading material, it's not always easy reading. More than once I've wanted to introduce someone to the topics, but couldn't hope for them to dig through a pile of essays.
This is an attempt to trim some of the most important texts down into something very concise and approachable. All of the original texts are well worth reading, or I wouldn't be summarizing them. I make no claim to be able to do them justice, but I can try to optimize them for different readers.
Akash has written a much shorter summary of all highlights.
Images generated by Midjourney, prompted by the post title.
----------------------------------------
The Lens That Sees Its Flaws
Full Text by Eliezer Yudkowsky
When you look at an optical illusion, you're aware that what you're seeing doesn't match reality. As a human, you have the exceptional ability to be able to understand this, that your mental model of the world is not the same as the actual world around you. You are seeing a warped image through a flawed lens. Because you know this, you can manually correct yourself - "no, it's not actually moving" - and have a more accurate model than you would have on autopilot.
Our brains are riddled with systematic errors, mistakes people make so often you could bet money on it. But brains are not magical. The systems making those errors can be understood, anticipated, and corrected for.
The human brain is a flawed lens that can see its own flaws. By learning, noticing, and correcting for distortions, the lens can become far more powerful.
----------------------------------------
What Do We Mean By "Rationality"?
Full Text by Eliezer Yudkowsky
Rationality is about being right and succeeding.
You think you have milk in the fridge when you don't, and when you come home milkless from shopping you're disappointed. You had a false belief. Your mental map of the world didn't match reality, and so you're steered into a |
5e21573e-fd38-474c-b173-0a7270eb01b1 | trentmkelly/LessWrong-43k | LessWrong | Musical Outgroups
[Content warning: Politics. Something I will regret writing. Cross-posted from Grand, Unified, Empty.]
A lot of this extends from Scott Alexander’s I Can Tolerate Anything Except the Outgroup, but if you don’t want to read the whole thing I’ll quote a few key definitions up front. Specifically:
> The Red Tribe is most classically typified by conservative political beliefs, strong evangelical religious beliefs, creationism, opposing gay marriage, owning guns, eating steak, drinking Coca-Cola, driving SUVs, watching lots of TV, enjoying American football, getting conspicuously upset about terrorists and commies, marrying early, divorcing early, shouting “USA IS NUMBER ONE!!!”, and listening to country music.
> The Blue Tribe is most classically typified by liberal political beliefs, vague agnosticism, supporting gay rights, thinking guns are barbaric, eating arugula, drinking fancy bottled water, driving Priuses, reading lots of books, being highly educated, mocking American football, feeling vaguely like they should like soccer but never really being able to get into it, getting conspicuously upset about sexists and bigots, marrying later, constantly pointing out how much more civilized European countries are than America, and listening to “everything except country”.
> (There is a partly-formed attempt to spin off a Grey Tribe typified by libertarian political beliefs, Dawkins-style atheism, vague annoyance that the question of gay rights even comes up, eating paleo, drinking Soylent, calling in rides on Uber, reading lots of blogs, calling American football “sportsball”, getting conspicuously upset about the War on Drugs and the NSA, and listening to filk – but for our current purposes this is a distraction and they can safely be considered part of the Blue Tribe most of the time)
And then the kicker:
> And my hypothesis, stated plainly, is that if you’re part of the Blue Tribe, then your outgroup isn’t al-Qaeda, or Muslims, or blacks, or gays, or transpeople |
a8d2a787-058c-4802-9fe8-a6ea890ed3a9 | trentmkelly/LessWrong-43k | LessWrong | Creating a Discord server for Mechanistic Interpretability Projects
TL;DR: I think there likely are a lot of people who want to work on mechanistic interpretability projects but couldn’t get into AI safety camp, so I created a Discord server for people to organize themselves into such projects. I’m going to lead one of them.
Why?
Many people interested in mechanistic interpretability projects were unable to get into AI safety camp. According to Linda Lisenfors, one of the main bottlenecks was a lack of project proposals.
The most popular project at AI safety camp was on understanding search in Transformers, with 46 people selecting it as their first choice. This suggests significant interest in mechanistic interpretability projects.
Moreover, I think that many mechanistic interpretability projects are low-hanging fruit that don’t require lots of experience or specific knowledge to execute. Anyone with basic CS skills can probably learn what they need to contribute along the way.
Mechanistic Interpretability Group
All in all, it would be a shame if people who are interested in working on mechanistic interpretability end up not doing so due to a lack of available projects and project leads.
With that in mind, I have created a Discord server to encourage people to propose and organize their own projects. You can join here: https://discord.gg/cMr5YqbU4y
This Discord server aims to help interested individuals with forming project teams, whilst being provided with guidance from other researchers in the area. You are welcome to join even if you don’t think you have what it takes to participate in such projects: it is also a place to learn and discover beginner-friendly resources. You can also check out Neel Nanda's guide to getting started on the field.
Algorithm distillation project
I’m also organizing a project on interpreting models that use the algorithm distillation setup. If you are interested, join the Discord server and go to the #algorithm-distillation-project channel to indicate your willingness to participate.
The pro |
55f482f4-39c4-4611-a6b1-7e32eee7141c | trentmkelly/LessWrong-43k | LessWrong | Robin Hanson on whether governments can squash COVID-19
Summary: Hanson argues that Western governments are unlikely to be competent enough to both squash COVID-19 and prevent new cases from entering from neighbouring lax countries. Final two paragraphs:
> Before we all jump off this cliff together, can we at least collect and publish some honest estimates of our chances of success? Such as perhaps via conditional betting markets? If you aren’t willing to exactly copy the whole China policy, or have them manage it, how serious could you really be about succeess?
>
> Look, this is like starting a war. Its not enough to ask “would it be nice to win such a war”, we need to ask “can we actually win?” Don’t start what you can’t finish. |
1b6e5cca-9c1a-4441-8c3b-19b13cb9d10b | StampyAI/alignment-research-dataset/lesswrong | LessWrong | A Proof Against Oracle AI
Armstrong et al. [suggest](http://www.aleph.se/papers/oracleAI.pdf) that an Oracle AI could be a solution to confine the harmful potential of artificial intelligence.
While the benefits are certainly considerable, I believe that even an oracle could lead to an existential risk, or at least to unpleasant situations.
I would like to share a *proof sketch* of the above:
For simplicity, let's consider an Oracle AI that has the ability to answer only yes / no to the questions posed by human operators. It is clear that here we are talking about an even weaker version than the one suggested by Armstrong, Bostrom and Sandberg. We define the Oracle as a superintelligent agent with the aim of maximizing some function .mjx-chtml {display: inline-block; line-height: 0; text-indent: 0; text-align: left; text-transform: none; font-style: normal; font-weight: normal; font-size: 100%; font-size-adjust: none; letter-spacing: normal; word-wrap: normal; word-spacing: normal; white-space: nowrap; float: none; direction: ltr; max-width: none; max-height: none; min-width: 0; min-height: 0; border: 0; margin: 0; padding: 1px 0}
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ϕ. Suppose that for a number of steps, from 0 to n, the oracle collaborates with human, always responding correctly to gain their trust. At some time t, the oracle knows which is the most optimized version of ϕ (what is the procedure to follow in order to obtain the desired goal).
Now a procedure is nothing but an algorithm (a set of rules) and as such can be encoded in a binary string of 0 and 1. So we have that at time t, oracle O knows ϕ and ϕ∈{0,1}n assuming the procedure has finite cardinality i.e. it will eventually halt, leading to the expected result. From this point on, O begins a strategic game against humans to get them to perform ϕ. If the history of all the answers since O was started is encoded in the string ψ , O need to include ϕ at a certain point in ψ. Since O is a Superintelligence and since every string can be reconstructed by only answering yes or no to questions like "is the first bit 1?" given that O has the complete trust of humans (and even if it falters it could return to behave correctly, adjusting the aim over and over again), eventually it can lead humans to act based on its responses and eventually to implement ϕ. Note that in all of this humans dont have the same overview and planning capacity of the Oracle and therefore they may not realize that, with their actions, they have set dangerous situations in motion. |
7e1ebc80-ddd4-43cf-b2ce-c8fb683ac609 | trentmkelly/LessWrong-43k | LessWrong | Get Rich Slowly
On the last day of my MBA’s finance class, the professor admitted that very few us are ever going to use the formula for return-on-debt in our lives. Instead, for that class he gave us a single sheet of paper titled “Bill’s simple and suboptimal personal investment guide” and explained his simple and suboptimal personal investment strategy.
In the years since, I have not once used the formula for return-on-debt. I did, however, use Bill’s guide to set up my own investment account, and then one for my dad, and for my girlfriend, and for a couple of friends… and now I’m going to do the same for you.
A few disclaimers before we start:
1. I am not a certified investment advisor. In fact, I’m not a certified anything at all. Don’t sue me.
2. This guide is suboptimal. You can open your own brokerage account and replicate the ETF structures to avoid the 0.15% Vanguard fees, but I’m not going to tell how to do that because see point #1 above.
3. This guide is simple. A lot of people I know don’t invest their money at all because they think they entire universe of finance is beyond the grasp of mere mortals. I am going to start with some very basic concepts, which it turns out are all that is needed because investment isn’t actually that complicated. If you’re familiar with the basics and agree that diversified index funds are the way to go, you can skip the “Investment Basics” section and get to the second part where I detail my personal investment strategy.
4. Personal gain disclaimer: Wealthfront is the main platform, along with Schwab, that I use for investing my money. I’ll explain the reasons for this choice later in the post. Wealthfront isn’t paying me for the endorsement (nor are they aware of Putanumonit’s existence) but the link is my own personal referral link. Clicking it gives you a fee waiver for $15,000 and me a waiver for $5,000. Wealthfront’s fees are 0.25%, so if you use my link I get $12.5 (and a warm fuzzy feeling).
5. Both the platforms and inve |
19fed501-8895-403c-8338-d066e345ea80 | trentmkelly/LessWrong-43k | LessWrong | From GPT to AGI
Epistemic status: Shower thoughts / I have an idea, but not much knowledge
While the the smallest GPT-3 model (125M) has 12 attention layers, each with 12x 64-dimension heads, the largest GPT-3 model (175B) uses 96 attention layers, each with 96x 128-dimension heads.
I would expect that with increased model size it will be possible to increase the attention field by a lot without much need for additional AI insight.
In a guide for AI dungeon there's a description of a pin item that serves as the context for the story. GPT-3 seems to be good at understanding the goals that are set in the pin item to the point that it tries to achieve them faster then the person who wrote the guide desires.
If the attention field would be larger it would allow for multiple pin items and each pin item could be even larger.
In AI dungeon GPT-3 can't influence the content of the pin items but it would be possible to give the GPT-3 the ability to use console commands to write into pin items to be able to have memory abilities similar to the short-term and middle term memory that humans have.
The ability to interact with the unix console was already shown Natural Language Shell example on the OpenAI website.
At the beginning a resulting agent could be mentored like AI dungeon has mentoring of the AI. If the AI is able to query Google via the console, I would imagine that it could be effective at many tasks.
A lot of newspaper articles could be written by such an agent who scouts the internet for other information that's published on the topic and synthesizes available information. Cyberwar could also be done by such agents.
I'd be happy to hear what other people think about such an agent. |
8b0efc48-bd0c-4f26-92a7-41d6d1ac5b02 | trentmkelly/LessWrong-43k | LessWrong | To the Robobassinet and Progress
Most parents of small babies, if they could, would be happy to have someone gently cuddle, shush, and rock their baby back to sleep when they needed settling at night. Babies can't comfortably soothe themselves to sleep yet, but taking care of them is exhausting work.
Wealthy people have historically handled this problem by hiring nurses, but paying someone to spend the night looking after your baby can't ever be within reach for most people. On the other hand, these simple actions are a very good fit for automation. We can't automate everything: diaper changing and feeding are much more complicated, but soothing a baby to sleep is actually a good fit for a machine!
With our first two babies we coslept, swaddling them in an annex off the bed. Once they were old enough to roll over we stopped swaddling and moved them to a crib. When this worked well, the baby would wake, quietly snuffle, wake Julia, nurse, and go back to sleep. When it didn't work well I was doing a lot of walking, bouncing, patting, and shushing. And so much frustration when a baby who had fallen asleep in your arms would wake when you set them down. And Julia says she couldn't fully relax while sleeping because she needed to pay a little bit of continuing attention to not rolling onto the baby and keeping the covers clear. We were both very tired all the time.
With our newborn, we have an automatic "Snoo" bassinet, and works very well. You swaddle the baby and clip them into the bassinet so they can't roll over. When you turn it on, it plays white noise and gently swivels to rock the baby to sleep. It listens to the noises the baby makes, and if they're not settling it swivels a bit more vigorously and plays louder white noise. If they still don't settle after a few escalations, though, it gives up and you come and figure out whether the baby needs food, a new diaper, or something else. We only have five nights of experience with it, but it seems to work very well and the ideas behind it make se |
db3d91e7-809d-4cbe-97de-a4b0949af29b | trentmkelly/LessWrong-43k | LessWrong | A Normative Rule for Decision-Changing Metrics
Yesterday I wrote about the difficulties of ethics and potential people. Namely, that whether you bring a person into existence or not changes the moral metric by which your decision is measured. At first all I had was the observation suggesting that the issue was complex, but no answer to the question "Well then, what should we do?" I will write now about an answer that came to me.
All theories regarding potential people start by comparing outcomes to find which is most desirable, then moving towards it. However I believe I have shown that there are two metrics regarding such questions, and those metrics can disagree. What then do we do?
We are always in a particular population ourselves, and so we can ask not which outcome is preferable, but if we should move from one situation to another. This allows us to consider the alternate metrics in series. For an initial name more attractive than "my rule" I will refer to the system as Deontological Consequentialism, or DC. I'm open to other suggestions.
Step 1: Consider your action with the metric of new people not coming to be: that is, only the welfare of the people who will exist regardless of your decision.* I will assume in this discussion there are three possibilities: people receive higher utility, lower utility, or effectively unchanged utility. You might dispense with the third option, the results are similar.
First, if you expect reduced utility for existing people from taking an action: do not take that action. This is regardless of how many new people might otherwise exist or how much utility they might have; if we never bring them into existence, we have wronged no one.
This is the least intuitive aspect of this system, though it is also the most critical for avoiding the paradoxes of which I am aware. I think this unintuitive nature mostly stems from automatically considering future people as if they exist. I'd also note that our intuitions are really not used to dealing with this sort of question, but |
d082f5db-3f8d-4161-bf0d-766063be3e54 | StampyAI/alignment-research-dataset/arxiv | Arxiv | Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents.
1 Introduction
---------------
Large language models (LLMs) have made impressive advances in language generation and understanding in recent years (Devlin et al., [2018](#bib.bib10); Radford et al., [2019](#bib.bib33); Raffel et al., [2019](#bib.bib34); Brown et al., [2020](#bib.bib5)). See Bommasani et al. ([2021](#bib.bib4)) for a recent summary of their capabilities and impacts.
Being trained on large corpora of human-produced language, these models are thought to contain a lot of information about the world (Roberts et al., [2020](#bib.bib36); Li et al., [2021](#bib.bib20); BIG-bench collaboration, [2021](#bib.bib3)) - albeit in linguistic form.
We ask whether we can use such knowledge contained in LLMs not just for linguistic tasks, but to make goal-driven decisions that can be enacted in interactive, embodied environments.
But we are not simply interested in whether we can train models on a dataset of demonstrations collected for some specific environment – we are instead interested in whether LLMs *already contain* information necessary to accomplish goals without any additional training.
More specifically, we ask whether world knowledge about how to perform high-level tasks (such as “make breakfast”) can be expanded to a series of groundable actions (such as “open fridge”, “grab milk”, “close fridge”, etc) that can be executed in the environment. For our investigation, we use the recently proposed VirtualHome environment (Puig et al., [2018](#bib.bib32)). It can simulate a large variety of realistic human activities in a household environment and supports the ability to perform them via embodied actions defined with a verb-object syntax. However, due to the open-ended nature of the tasks, it is difficult to autonomously evaluate their success. We rely on human evaluation (conducted on Mechanical Turk) to decide whether sequences of actions meaningfully accomplish posed tasks.
We find that large GPT-3 (Brown et al., [2020](#bib.bib5)) and Codex (Chen et al., [2021](#bib.bib7)) models, when prompted with a single fixed example of a task description and its associated sequence of actions, can produce very plausible action plans for the task we’re interested in. Such completions reflect the information already stored in the model – no model fine-tuning is involved. Additionally, we only observe this effect in the larger models. Unfortunately, despite their semantic correctness, the produced action plans are often not executable in the environment. Produced actions may not map precisely to admissible actions, or may contain various linguistic ambiguities.
We propose several tools to improve executability of the model’s outputs. First, we enumerate all admissible actions and map the model’s output phrases to the most semantically-similar admissible action (we use similarity measure between sentence embeddings produced by a RoBERTa model Liu et al. ([2019](#bib.bib22)) in this work, but other choices are possible).
Second, we use the model to autoregressively generate actions in a plan by conditioning past actions that have been made admissible via the technique above. Such on-the-fly correction can keep generation anchored to admissible actions. Third, we provide weak supervision to the model by prompting the model with a known task example similar to the query task. This is somewhat reminiscent of prompt tuning approaches but does not require access to gradients or internals of the model.
Using the above tools to bias model generation, we find that we improve executability of action plans from 18% to 79% (see Figure [1](#S0.F1 "Figure 1 ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents")) without any invasive modifications to model parameters or any extra gradient or internal information beyond what is returned from the model’s forward pass. This is advantageous because it does not require any modifications to the model training procedure and can fit within existing model serving pipelines. However, we do find there to be some drop in correctness of the action sequences generated with the above tools (as judged by humans), indicating a promising step, but requiring more research on the topic.
To summarize, our paper’s contributions are as follows:
* We show that without any training, large language models can be prompted to generate plausible goal-driven action plans, but such plans are frequently not executable in interactive environments.
* We propose several tools to improve executability of the model generation without invasive probing or modifications to the model.
* We conduct a human evaluation of multiple techniques and models and report on the trade-offs between executability and semantic correctness.
Figure 2: We investigate the possibility of extracting actionable knowledge from pre-trained large language models (LLMs). We first show surprising finding that pre-trained causal LLMs can decompose high-level tasks into sensible low-level action plans (left). To make the plans executable, we propose to translate each step into admissible action via another pre-trained masked LLM (middle). The translated action is appended to the prompt used for generating the remaining steps (right). All models are kept frozen without additional training.
2 Evaluation Framework
-----------------------
Simulating open-ended tasks that resemble naturalistic human activities requires an environment to support a rich set of diverse interactions, rendering most existing embodied environments unsuitable for our investigation. One exception is VirtualHome (Puig et al., [2018](#bib.bib32)), which we evaluate on as it models complex human activities, though only in a household setting.
To measure correctness of the generated action plans, for which evaluating computationally is inherently difficult for these open-ended tasks, we conduct a human evaluation similar to Puig et al. ([2018](#bib.bib32)). We note that since no further training is involved throughout our investigations, the observations and findings presented in this paper should also translate to similar embodied environments, likely even beyond the household domain.
###
2.1 Evaluated Environment: VirtualHome
#### Preliminaries
In VirtualHome, activities are expressed as programs. Each program consists of a sequence of textual action steps, where each step is written as:
[action] ⟨arg⟩(idx).
Each action refers to one of the 42 atomic actions supported in VirtualHome, such as “walk” and “open”. Full list of atomic actions can be found in Appendix [A.4](#A1.SS4 "A.4 Natural Language Templates for All Atomic Actions ‣ Appendix A Appendix ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Different actions take in different numbers of arg, such as “bedroom” and “fridge”, that are necessary for specifying an interaction. Associated with each arg is a unique id specifying the corresponding node in the environment graph, in case of multiple instances of the same object class are present in the graph. For the sake of simplicity, we omit the id in the remaining discussions of this paper and allow automatic assignment by the environment. An example program is shown below for the task “Relax on sofa”:
| |
| --- |
| [WALK] ⟨living\_room⟩(1) |
| [WALK] ⟨television⟩(1) |
| [FIND] ⟨television⟩(1) |
| [SWITCHON] ⟨television⟩(1) |
| [FIND] ⟨sofa⟩(1) |
| [SIT] ⟨sofa⟩(1) |
| [TURNTO] ⟨television⟩(1) |
| [WATCH] ⟨television⟩(1) |
#### Evaluated Tasks
We use the ActivityPrograms knowledge base collected by Puig et al. ([2018](#bib.bib32)) for evaluation. It contains 2821 different entries annotated by Amazon Mechanical Turk (MTurk) workers. Each entry contains 1) a high-level task name (e.g. “Watch TV”), 2) detailed instructions expressed in natural language to complete the task (e.g. “Sit on my couch directly opposite my TV, switch on my TV with the remote control and watch”), and 3) an executable program containing all necessary steps for a robotic agent (example above). We omit the use of detailed instructions (2) as we desire direct extraction of executable programs (3) from only high-level task names (1). There are 292 distinct high-level tasks in the knowledge base, from which we randomly sample 88 held-out tasks for evaluation. The remaining 204 tasks are used as demonstration set from which we are allowed to select as example(s) for prompting language models, or in the case of supervised fine-tuning baselines, they are used to fine-tune pre-trained language models.
Notation Summary:
LMP: text completion language model (also referred as Planning LM)
LMT: text embedding language model (also referred as Translation LM)
{(Ti,Ei)}Ni=1: demonstration set, where T is task name and E is example plan for T
C: cosine similarity function
P: mean token log probability under LMP
Input: query task name Q, e.g. “make breakfast”
Output: action plan consisting of admissible env actions, e.g. “open fridge”
Extract most similar example (T∗,E∗) whose T∗ maximizes C(LMT(T),LMT(Q))
Initialize prompt with (T∗+E∗+Q)
while max step is not reached do
Sample LMP with current prompt to obtain k single-step action phrases
for each sample ^a and each admissible env action ae do
Calculate ranking score by C(LMT(^a),LMT(ae))+β⋅P(^a)
end for
Append highest-scoring env action a∗e to prompt
Append a∗e to output
if >50% samples are 0-length or highest score <ϵ then
break
end if
end while
Algorithm 1 Generating Action Plans from Pre-Trained Language Models
###
2.2 Metrics
A program that commands the agent to wander around in a household environment is highly executable but is mostly not correct. On the other hand, a program composed of natural language instructions annotated by humans is likely correct but cannot be executed, because its format is ambiguous and may lack necessary common-sense actions (e.g. fridge must be opened before an agent can grab things from it). We thus consider two axes for evaluation: executability and correctness.
#### Executability
Executability measures whether an action plan can be correctly parsed and satisfies the common-sense constraints of the environment. To be correctly parsed, an action plan must be syntactically correct and contain only allowed actions and recognizable objects. To satisfy the common-sense constraints, each action step must not violate the set of its pre-conditions (e.g. the agent cannot grab milk from the fridge before opening it) and post-conditions (e.g. the state of the fridge changes from “closed” to “open” after the agent opens it). We report the average executability across all 88 tasks and all 7 VirtualHome scenes.
#### Correctness
Unlike most embodied environments where the completion of a task can be easily judged, the ambiguous and multimodal nature of natural language task specification makes it impractical to obtain a gold-standard measurement of correctness111One approach could be measuring the similarity of the final environment state produced by executing predicted and human-written programs, but initial state must be kept fixed for each task, which are not appropriate for many tasks due to their open-ended nature.. Therefore, we conduct human evaluations for the main methods. For the remaining analysis, we rely on a match-based metric that measures how similar a generated program is to human annotations. Specifically, we follow Puig et al. ([2018](#bib.bib32)) and calculate the longest common subsequence (LCS) between two programs, normalized by the maximum length of the two. In the presence of multiple human-written programs for a single task, we take the maximum LCS across them. However, we note that the majority of the tasks only have one human annotation, but there are often many plausible ways to complete a certain task, making this metric imperfect at evaluation program correctness222Although LCS has a mathematical range of [0,1], we measure the LCS between different human-written programs for the same task and find an empirical maximum of 0.489.. Although correlation between the two is shown by Puig et al. ([2018](#bib.bib32)), we consider it only as a proxy metric in replacement of unscalable human evaluation.
3 Method
---------
In this section, we investigate the possibility of extracting actionable knowledge from pre-trained language models without further training. We first give an overview of the common approach to query large language models (LLMs) and how it may be used for embodied agents in Section [3.1](#S3.SS1 "3.1 Querying LLMs for Action Plans ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Then we describe an inference-time procedure that addresses several deficiencies of the LLM baseline and offers better executability in embodied environments. We break down the proposed procedure into three individual components, each discussed in Section [3.2](#S3.SS2 "3.2 Admissible Action Parsing by Semantic Translation ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), [3.3](#S3.SS3 "3.3 Autoregressive Trajectory Correction ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), [3.4](#S3.SS4 "3.4 Dynamic Example Selection for Improved Knowledge Extraction ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Pseudo-code is in Algorithm [1](#alg1 "Algorithm 1 ‣ Evaluated Tasks ‣ 2.1 Evaluated Environment: VirtualHome ‣ 2 Evaluation Framework ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
Since LMs excel at dealing with natural language text instead of the specific format required by VirtualHome as described in Section [2.1](#S2.SS1 "2.1 Evaluated Environment: VirtualHome ‣ 2 Evaluation Framework ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), we only expose natural language text to LMs. To do this, we define a bi-directional mapping for each atomic action that converts between the natural language format and the program format. For instance, “walk to living room” is mapped to [WALK] ⟨living\_room⟩(1). Full list of the mappings is in Appendix [A.4](#A1.SS4 "A.4 Natural Language Templates for All Atomic Actions ‣ Appendix A Appendix ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
###
3.1 Querying LLMs for Action Plans
Previous works have shown that large language models pre-trained on a colossal amount of data would internalize rich world knowledge that can be probed to perform various downstream tasks (Radford et al., [2019](#bib.bib33); Brown et al., [2020](#bib.bib5)). Notably, autoregressive LLMs can even perform in-context learning, an ability to solve tasks using only contextual information without gradient updates (Brown et al., [2020](#bib.bib5)). Contextual information is given as part of the input prompt and LMs are asked to complete the remaining text. It often consists of natural language instructions and/or a number of examples containing the desired input/output pairs.
We adopt the same approach to query LLMs to generate action plans for high-level tasks. Specifically, we prepend one example high-level task and its annotated action plan from the demonstration set to the query task, as shown in Figure [2](#S1.F2 "Figure 2 ‣ 1 Introduction ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). To obtain text completion results, we sample from autoregressive LLM using temperature sampling and nucleus sampling (Holtzman et al., [2019](#bib.bib16)). We refer to this LM as Planning LM and the approach using this LM for plan generation as Vanilla ⟨LM⟩, where ⟨LM⟩ is replaced by specific language model such as GPT-3.
To improve the generation quality, we follow Chen et al. ([2021](#bib.bib7)) to sample multiple outputs for each query. However, unlike Chen et al. ([2021](#bib.bib7)) who investigate program synthesis and can choose the sample with highest unit test pass rate, we only consider the setting where one sample is allowed to be evaluated for each task. This is because repetitive trial-and-error
is equivalent to probing the environment for privileged information, which should not be considered viable in our setting.
For Vanilla ⟨LM⟩, to choose the best action plan X∗ among k samples (X1,X2,...,Xk), each consisting of ni tokens Xi=(xi,1,xi,2,...,xi,ni), we select the sample with highest mean log probability as follows:
| | | | |
| --- | --- | --- | --- |
| | argmaxXi(Pθ(Xi):=1nini∑j=1logpθ(xi,j|xi,<j))whereθparameterizes the Planning LM. | | (1) |
###
3.2 Admissible Action Parsing by Semantic Translation
One issue arises when naively following the above approach to generate action plans: the plan expressed in free-form language often cannot be mapped to unambiguous actionable steps and thus is not executable by a robotic agent.
Many reasons can cause such failures: 1) the output does not follow pre-defined mappings of any atomic action (e.g. “I first walk to the bedroom” is not of the format “walk to ⟨PLACE⟩”), 2) the output may refer to atomic action and objects using words unrecognizable by the environment (e.g. “microwave the chocolate milk” where “microwave” and “chocolate milk” cannot be mapped to precise action and object), or 3) the output contains lexically ambiguous words (e.g. “open TV” should instead be “switch on TV”).
Instead of developing a set of rules to transform the free-form text into admissible action steps, we propose to again leverage world knowledge learned by language models to semantically translate the action. For each admissible environment action ae, we calculate its semantic distance to the predicted action phrase ^a by cosine similarity:
| | | | |
| --- | --- | --- | --- |
| | C(f(^a),f(ae)):=f(^a)⋅f(ae)∥f(^a)∥∥f(ae)∥wherefis an embedding function. | | (2) |
To embed the output action phrase and environment actions, we use a BERT-style LM (Devlin et al., [2018](#bib.bib10); Liu et al., [2019](#bib.bib22)) pre-trained with Sentence-BERT (Reimers and Gurevych, [2019](#bib.bib35)) objective, to which we refer as Translation LM333Note that this is a different LM than the GPT-style Planning LM. Using a single LM for both purposes could as well be possible and likely more efficient, but we leave such investigation to future works..
The action embedding is obtained by mean-pooling the last layer hidden states across all tokens in that action phrase. While the set of admissible actions in our environment is discrete and possible to exhaustively enumerate, sampling or projection can be employed in larger discrete or continuous action spaces.
###
3.3 Autoregressive Trajectory Correction
Translating each step of the program after the entire program has been synthesized
lacks consideration of achievability of individual steps and subjects to compounding errors.
In practice, LLMs might output compounded instructions for a single step, even though it cannot be completed using one admissible action in the environment. To this end, we can instead interleave plan generation and action translation to allow for automatic trajectory correction. At each step, we first query Planning LM to generate k samples for a single action (^a1,^a2,...,^ak).
For each sample ^a, we consider both its semantic soundness and its achievability in the environment. Specifically, we aim to find admissible environment action ae by modifying the ranking scheme described in Equation [1](#S3.E1 "(1) ‣ 3.1 Querying LLMs for Action Plans ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") as follows:
| | | | |
| --- | --- | --- | --- |
| | argmaxae[max^aC(f(^a),f(ae))+β⋅Pθ(^a)]whereβis a weighting coefficient. | | (3) |
Then we append the translated environment action ae to the unfinished text completion. This way all subsequent steps will be conditioned on admissible actions instead of free-form action phrases generated by Planning LM. Furthermore, we can use Translation LM to detect out-of-distribution actions, those outside the capabilities of a robot, and terminate a program early instead of mapping to a faulty action. This can be achieved by setting a threshold ϵ such that if max^a,aeC(f(^a),f(ae))+β⋅Pθ(^a)<ϵ at step t, the program is terminated early. Since we now sample Planning LM for individual steps instead of an entire sequence, another termination condition we consider is when >50% of current-step samples are 0-length (excluding leading or trailing non-English text tokens).
###
3.4 Dynamic Example Selection for Improved Knowledge Extraction
So far in the text, we always give the same example in the prompt for all query tasks. However, consider the task of “ordering pizza”. Prompting LLMs with this task may give the assumption that the agent is initialized in front of a computer, and the LLMs may guide the agent to search for a pizza store and click “checkout my cart”. Although these are reasonable and feasible in the real world, such assumption cannot always be made as these interactions may not be supported in simulated environments. In fact, the closest series of actions that human experts give in VirtualHome may be “walking to a computer”, “switching on the computer”, and “typing the keyboard”. Without being fine-tuned on these data, LLMs would often fail at these tasks.
To provide weak supervision at inference time, we propose to select the most similar task T and its example plan E from the demonstration set to be used as the example in the prompt. Specifically, we re-use the same Translation LM introduced in Section [3.2](#S3.SS2 "3.2 Admissible Action Parsing by Semantic Translation ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") and select (T∗,E∗) whose high-level task name T∗ maximizes C(f(T),f(Q)), where Q is the query task. An example is shown in Figure [2](#S1.F2 "Figure 2 ‣ 1 Introduction ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") where “Shave” is the most similar to the query task “Apply lotion”.
#### Final Method
Combining the various improvement discussed above, we refer to the final method as
Translated ⟨LM⟩
, where ⟨LM⟩ is replaced by specific language model used such as GPT-3.
Figure 3: Visualization of VirtualHome programs generated by our approach. The top row shows the execution of the task “Complete Amazon Turk Surveys”, and the bottom row shows the task “Get Glass of Milk”. We show LLMs not only can generate sensible action plans given only high-level tasks but also contains the actionable knowledge that can be extracted for grounding in embodied environments.
4 Results
----------
In this section, we first show that language models can generate sensible action plans for many high-level tasks, even without any additional training. Then we highlight its inadequacy when naively applied to embodied environments and demonstrate how this can be improved by again leveraging world knowledge learned by LLMs. Visualization of generated programs is shown in Figure [3](#S3.F3 "Figure 3 ‣ Final Method ‣ 3.4 Dynamic Example Selection for Improved Knowledge Extraction ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
#### Sampling from LMs
Pre-trained LMs are sensitive to sampling parameters and the specific example given in the prompt. For all evaluated methods, we perform hyperparameter search over various sampling parameters, and for methods using a fixed prompt example, we report metrics averaged across three randomly chosen examples.
To select the best run for each method, we rank the runs by the sum of LCS and executability, each normalized by human-expert scores. Further details are in Appendix [A.1](#A1.SS1 "A.1 Hyperparameter Search ‣ Appendix A Appendix ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
#### Model Choices
For Planning LM, we evaluate a representative set of causal language models. For Translation LM, we mainly use Sentence-RoBERTa-355M and provide relevant ablations in Section [5.3](#S5.SS3 "5.3 Effect of Different Translation LMs ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
GPT-3 and Codex are accessed using OpenAI API, and the remaining models are accessed through open-source packages, Hugging Face Transformers (Wolf et al., [2019](#bib.bib48))
and SentenceTransformers (Reimers and Gurevych, [2019](#bib.bib35)), all without additional training (except for the fine-tuning baseline).
| | | | |
| --- | --- | --- | --- |
| Language Model | Executability | LCS | Correctness |
| Vanilla GPT-2 117M | 18.66% | 3.19% | 15.81% (4.90%) |
| Vanilla GPT-2 1.5B | 39.40% | 7.78% | 29.25% (5.28%) |
| Vanilla Codex 2.5B | 17.62% | 15.57% | 63.08% (7.12%) |
| Vanilla GPT-Neo 2.7B | 29.92% | 11.52% | 65.29% (9.08%) |
| Vanilla Codex 12B | 18.07% | 16.97% | 64.87% (5.41%) |
| Vanilla GPT-3 13B | 25.87% | 13.40% | 49.44% (8.14%) |
| Vanilla GPT-3 175B | 7.79% | 17.82% | 77.86% (6.42%) |
| Human | 100.00% | N/A | 70.05% (5.44%) |
| Fine-tuned GPT-3 13B | 66.07% | 34.08% | 64.92% (5.96%) |
| Our Final Methods | | | |
| Translated Codex 12B | 78.57% | 24.72% | 54.88% (5.90%) |
| Translated GPT-3 175B | 73.05% | 24.09% | 66.13% (8.38%) |
Table 1: Human-evaluated correctness and evaluation results in VirtualHome. Although action plans generated by large language models can match or even surpass human-written plans in correctness measure, they are rarely executable. By translating the naive action plans, we show an important step towards grounding LLMs in embodied environments, but we observe room to achieve this without trading executability for correctness. We also observe a failure mode among smaller models that lead to high executability. For correctness measure, standard error of the mean across 10 human annotators is reported in the parenthesis.
###
4.1 Do LLMs contain actionable knowledge for high-level tasks?
We first investigate whether LLMs can generate sensible action plans expressed in free-form language. We use the approach described in Section [3.1](#S3.SS1 "3.1 Querying LLMs for Action Plans ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") to query pre-trained LLMs. To evaluate the correctness of generated action plans, we conduct human evaluations.
For each model, we ask 10 human annotators to determine -- by answering ‘‘Yes’’ or ‘‘No’’ -- whether each task can be completed using provided action steps. To provide a reference of how humans might rate the action plans provided by other humans, we also ask annotators to rate the human-written action plans included in the VirtualHome dataset for the same set of tasks. In contrast to the free-form text output by LLMs, humans wrote the plans using a graphical programming interface that enforces strict syntax and a chosen set of atomic action vocabulary, which limit the expressivity and the completeness of their answers444 Puig et al. ([2018](#bib.bib32)) also conduct a human evaluation on 100 randomly sampled human-written programs and show that 64% of them are complete (i.e. contain all necessary steps). Readers are encouraged to refer to Puig et al. ([2018](#bib.bib32)) for a more comprehensive analysis of the dataset.. More details of our human evaluation procedure can be found in Appendix [A.2](#A1.SS2 "A.2 Details of Human Evaluations ‣ Appendix A Appendix ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
We show the human evaluation results in Figure [1](#S0.F1 "Figure 1 ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), where the y-axis shows correctness averaged across all tasks and all annotators. Surprisingly, when LLMs are large enough and without imposed syntactic constraints, they can generate highly realistic action plans whose correctness – as deemed by human annotators – even surpasses human-written action plans.
We also observe some level of correctness for smaller models such as GPT-2. However, inspection of its produced output indicates that it often generates shorter plans by ignoring common-sense actions or by simply rephrasing the given task (e.g. the task “Go to sleep” produces only a single step “Go to bed”). These failure modes sometimes mislead human annotators to mark them correct as the annotators may ignore common-sense actions in their judgment as well, resulting in a higher correctness rate than the quality of the output shows.
###
4.2 How executable are the LLM action plans?
We analyze the executability of LLM plans by evaluating them in all 7 household scenes in VirtualHome. As shown in Table [1](#S4.T1 "Table 1 ‣ Model Choices ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), we find action plans generated naively by LLMs are generally not very executable. Although smaller models seem to have higher executability, we find that the majority of these executable plans are produced by ignoring the queried task and repeating the given example of a different task. This is validated by the fact that smaller models have lower LCS than larger models despite having high executability, showing that this failure mode is prevalent among smaller models. In contrast, larger models do not suffer severely from this failure mode. Yet as a result of being more expressive, their generated programs are substantially less executable.
###
4.3 Can LLM action plans be made executable by proposed procedure?
We evaluate the effectiveness of our proposed procedure of action translation. We first create a bank of all allowed 47522 action steps in the environment, including all possible combinations of atomic actions and allowed arguments/objects. Then we use an off-the-shelf Sentence-RoBERTa (Liu et al., [2019](#bib.bib22); Reimers and Gurevych, [2019](#bib.bib35)) as Translation LM to create embeddings for actions and output text. For better computational efficiency, we pre-compute the embeddings for all allowed actions, leaving minor computation overhead for our procedure over the baseline methods at inference time. As shown in Table [1](#S4.T1 "Table 1 ‣ Model Choices ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), executability of generated programs is significantly improved. Furthermore, we also observe improved LCS because the translated action steps precisely follow the program syntax and thus are more similar to the plans produced by human experts. Sample output is shown in Figure [1](#S0.F1 "Figure 1 ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") and a larger random subset of generated samples can be found in Appendix [A.5](#A1.SS5 "A.5 Random Samples of Action Plans ‣ Appendix A Appendix ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
To validate their correctness, we again perform human evaluations using the same procedure from Section [4.1](#S4.SS1 "4.1 Do LLMs contain actionable knowledge for high-level tasks? ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Results are shown in Table [1](#S4.T1 "Table 1 ‣ Model Choices ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). We find that despite being more similar to human-written plans as they follow strict syntax, the programs are deemed less correct by humans compared to their vanilla counterparts. By examining the output, we observe two main sources of errors. First, we find Translation LM is poor at mapping compounded instructions to a succinct admissible action, e.g. “brush teeth with toothbrush and toothpaste”.
Second, we find that the generated programs are sometimes terminated too early. This is partly due to the imperfect expressivity of the environment; certain necessary actions or objects are not implemented to fully achieve some tasks, so Translation LM cannot map to a sufficiently similar action. This is also reflected by our human evaluation results of the programs written by other humans, as only 70% of the programs are considered complete.
5 Analysis and Discussions
---------------------------
###
5.1 Ablation of design decisions
We perform ablation studies for the three components of our proposed procedure, described in Section [3.2](#S3.SS2 "3.2 Admissible Action Parsing by Semantic Translation ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), [3.3](#S3.SS3 "3.3 Autoregressive Trajectory Correction ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), and [3.4](#S3.SS4 "3.4 Dynamic Example Selection for Improved Knowledge Extraction ‣ 3 Method ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") respectively. As shown in Table [2](#S5.T2 "Table 2 ‣ 5.1 Ablation of design decisions ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), leaving out any of the three components would all lead to decreased performance in both executability and LCS. An exception is Translated GPT-3 w/o Trajectory Correction, where we observe a slight improvement in LCS at the expense of a considerable drop in executability. Among the three proposed components, leaving out action translation leads to the most significant executability drop, showing the importance of action translation in extracting executable action plans from LLMs.
| Methods | Executability | LCS |
| --- | --- | --- |
| Translated Codex 12B | 78.57% | 24.72% |
| - w/o Action Translation | 31.49% | 22.53% |
| - w/o Dynamic Example | 50.86% | 22.84% |
| - w/o Trajectory Correction | 55.19% | 24.43% |
| Translated GPT-3 175B | 73.05% | 24.09% |
| - w/o Action Translation | 36.04% | 24.31% |
| - w/o Dynamic Example | 60.82% | 22.92% |
| - w/o Trajectory Correction | 40.10% | 24.98% |
Table 2: Ablation of three proposed techniques.
###
5.2 Are the generated action plans grounded in the environment?
Since successful execution of correct action plans directly measures grounding, we calculate the percentage of generated action plans that are both correct and executable. We deem an action plan to be correct if 70% or more human annotators decide it is correct. Human-written plans are 100% executable, of which 65.91% are deemed correct. Results for LMs are shown in Figure [4](#S5.F4 "Figure 4 ‣ 5.2 Are the generated action plans grounded in the environment? ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
Although smaller LMs such as GPT-2 can generate highly executable action plans as shown in Table [1](#S4.T1 "Table 1 ‣ Model Choices ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), these executable plans mostly are not correct, as they often repeat the given example or do not contain all necessary steps. Increasing model parameters can lead to some improvement in generating plans that are both executable and correct, yet it scales poorly with the parameter count. In the meantime, action translation offers a promising way towards grounding actionable knowledge by producing executable and correct plans, though a large gap remains to be closed to reach human-level performance (65.91%).
Figure 4: Percentage of both executable and correct action plans generated by LMs.
###
5.3 Effect of Different Translation LMs
In this section, we study the effect of using different Translation LM. We compare two size variants of Sentence BERT and Sentence RoBERTa (Devlin et al., [2018](#bib.bib10); Liu et al., [2019](#bib.bib22); Reimers and Gurevych, [2019](#bib.bib35)) trained on the STS benchmark (Cer et al., [2017](#bib.bib6)) and a baseline using averaged GloVe embeddings (Pennington et al., [2014](#bib.bib30)). Results are shown in Table [3](#S5.T3 "Table 3 ‣ 5.3 Effect of Different Translation LMs ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Notably, we do not observe significant differences in executability and LCS across different variants of BERT and RoBERTa. We hypothesize that this is because any language models trained on reasonably large datasets should be capable of the single-step action phrase translation considered in this work. However, simply using average GloVe embeddings would lead to significantly reduced performance.
| Translation LM | Parameter Count | Executability | LCS |
| --- | --- | --- | --- |
| Codex 12B as Planning LM | | | |
| Avg. GloVe embeddings | - | 46.92% | 9.71% |
| Sentence Bert (base) | 110M | 73.21% | 24.10% |
| Sentence Bert (large) | 340M | 75.16% | 20.79% |
| Sentence RoBERTa (base) | 125M | 74.35% | 22.82% |
| Sentence RoBERTa (large) | 325M | 78.57% | 24.72% |
| GPT-3 175B as Planning LM | | | |
| Avg. GloVe embeddings | - | 47.40% | 12.16% |
| Sentence Bert (base) | 110M | 77.60% | 24.49% |
| Sentence Bert (large) | 340M | 67.86% | 21.24% |
| Sentence RoBERTa (base) | 125M | 72.73% | 23.64% |
| Sentence RoBERTa (large) | 325M | 73.05% | 24.09% |
Table 3: Effect of different Translation LMs on executability and LCS.
###
5.4 Can LLMs generate actionable programs by following step-by-step instructions?
Prior works often focus on translating step-by-step instructions into executable programs.
Specifically, instead of only providing a high-level task name, how-to instructions are also provided, as shown in Figure [6](#S5.F6 "Figure 6 ‣ 5.4 Can LLMs generate actionable programs by following step-by-step instructions? ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents").
Although this setting is easier as it does not require rich prior knowledge, how-to instructions can help resolve much ambiguity of exactly how to perform a high-level task when multiple solutions are possible.
To investigate whether pre-trained LLMs are capable of doing this without additional training, we include these instructions in the prompt and evaluate LLMs with the proposed procedure.
We compare to a supervised baseline from VirtualHome that trains an LSTM (Hochreiter and Schmidhuber, [1997](#bib.bib15)) from scratch on human-annotated data.
Since the code to train the baseline is not publicly released and a different train/test split is likely used, we only show results reported in Puig et al. ([2018](#bib.bib32)) as a crude reference. We also cannot compare executability as it is not reported.
Results are shown in Table [6](#S5.F6 "Figure 6 ‣ 5.4 Can LLMs generate actionable programs by following step-by-step instructions? ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Surprisingly, without being fine-tuned on any domain data, Translated Codex/GPT-3 can attain LCS close to supervised methods while generating highly executable programs.
{floatrow}\ffigbox
Figure 5: An example prompt containing step-by-step instructions.\capbtabbox
| Methods | Executability | LCS |
| --- | --- | --- |
| Translated Codex 12B | 78.57% | 32.87% |
| Translated GPT-3 175B | 74.15% | 31.05% |
| Supervised LSTM | - | 34.00% |
Figure 6: Executability and LCS when conditioned on step-by-step instructions.
###
5.5 Analysis of program length
Shorter programs have a natural advantage of being more executable as they need to satisfy less pre/post-conditions, albeit being prone to incompleteness. To validate the proposed approach does not simply generate very short programs, we calculate the average program length across the 88 evaluated tasks. Results are shown in Table [4](#S5.T4 "Table 4 ‣ 5.5 Analysis of program length ‣ 5 Analysis and Discussions ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"). Mirroring the observations made in Section [4.1](#S4.SS1 "4.1 Do LLMs contain actionable knowledge for high-level tasks? ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents") and Section [4.2](#S4.SS2 "4.2 How executable are the LLM action plans? ‣ 4 Results ‣ Language Models as Zero-Shot Planners: Extracting Actionable Knowledge for Embodied Agents"), we find smaller LMs such as GPT-2 tend to generate shorter programs than larger models do while frequently repeating the given executable example. In contrast, larger models like Codex and GPT-3 can generate more expressive programs with high realism, yet consequently, they often suffer from executability. We show proposed procedure can find appropriate balance and is capable of generating programs that are highly executable while maintaining reasonable expressiveness as measured by program length.
| Methods | Executability | Average Length |
| --- | --- | --- |
| Vanilla GPT-2 1.5B | 39.40% | 4.24 |
| Vanilla Codex 12B | 18.07% | 7.22 |
| Vanilla GPT-3 175B | 7.79% | 9.716 |
| Translated Codex 12B | 78.57% | 7.13 |
| Translated GPT-3 175B | 73.05% | 7.36 |
| Human | 100.00% | 9.66 |
Table 4: Average executability & program length of different methods.
6 Related Works
----------------
Large-scale natural language modeling has witnessed rapid advances since the inception of the Transformer architecture (Vaswani et al., [2017](#bib.bib46)). It has been shown by recent works that large language models (LLMs) pre-trained on large unstructured text corpus not only can perform strongly on various down-stream NLP tasks (Devlin et al., [2018](#bib.bib10); Radford et al., [2019](#bib.bib33); Raffel et al., [2019](#bib.bib34); Brown et al., [2020](#bib.bib5)) but the learned representations can also be used to model relations of entities (Li et al., [2021](#bib.bib20)), retrieve matching visual features (Ilharco et al., [2020](#bib.bib17)), synthesize code from docstrings (Hendrycks et al., [2021](#bib.bib13); Chen et al., [2021](#bib.bib7)), solve math problems (Cobbe et al., [2021](#bib.bib8); Shen et al., [2021](#bib.bib39)), and even as valuable priors when applied to diverse tasks from different modalities (Lu et al., [2021](#bib.bib23); Tsimpoukelli et al., [2021](#bib.bib45)).
Notably, by pre-training on large-scale data, these models can also internalize an implicit knowledge base containing rich information about the world from which factual answers (e.g. “Dante was born in ⟨PLACE⟩”) can be extracted (Petroni et al., [2019](#bib.bib31); Jiang et al., [2020](#bib.bib18); Davison et al., [2019](#bib.bib9); Talmor et al., [2020](#bib.bib43); Roberts et al., [2020](#bib.bib36)). Compared to prior works in single-step knowledge extraction, we aim to extract sequential action plans to complete open-ended human activities while satisfying various constraints of an interactive environment.
Many prior works have looked into grounding natural language in embodied environments.
A series of them parse language instructions into formal logic or rely mainly on lexical analysis to resolve various linguistic ambiguities for embodied agents (Artzi and Zettlemoyer, [2013](#bib.bib2); Misra et al., [2015](#bib.bib28), [2016](#bib.bib29); Tenorth et al., [2010](#bib.bib44)). However, they often require many hand-designed rules or scale inadequately to more complex tasks and environments. Recently, many efforts have been put into creating more realistic environments with the goal to further advances in this area (Puig et al., [2018](#bib.bib32); Shridhar et al., [2020a](#bib.bib40), [b](#bib.bib41); Kolve et al., [2017](#bib.bib19); Savva et al., [2019](#bib.bib37); Anderson et al., [2018](#bib.bib1)). At the same time, by leveraging the better representation power of neural architectures, a number of works have looked into creating instruction-following agents that can perform manipulation (Lynch and Sermanet, [2020](#bib.bib24), [2021](#bib.bib25)), navigation (Fried et al., [2018](#bib.bib11); Wang et al., [2019](#bib.bib47); Majumdar et al., [2020](#bib.bib26)), or both (Suglia et al., [2021](#bib.bib42); Hill et al., [2020](#bib.bib14); Fu et al., [2019](#bib.bib12)). Recent works also use language as hierarchical abstractions to plan actions using imitation learning (Sharma et al., [2021](#bib.bib38)) and to guide exploration in reinforcement learning (Mirchandani et al., [2021](#bib.bib27)).
Notably, many prior works do not leverage full-blown pre-trained LLMs. Perhaps more importantly, few works have evaluated LLMs in an embodiment setting that realizes the full potential of the actionable knowledge these models already contain by pre-training on large-scale unstructured text: the tasks evaluated are often generated from a handful of templates, which do not resemble the highly diverse activities that humans perform in daily lives.
The development of VirtualHome environment (Puig et al., [2018](#bib.bib32)) enables such possibility. However, relevant works (Puig et al., [2018](#bib.bib32); Liao et al., [2019](#bib.bib21)) rely on human-annotated data and perform supervised training from scratch. Due to the lack of rich world knowledge, these models can only generate action plans given detailed instructions of how to act or video demonstrations. In this work, we take a step further by conditioning only on the high-level descriptions and by extracting executable action plans from LLMs without any additional training.
7 Limitations and Conclusion
-----------------------------
There are several notable limitations of this work. First, although our approach presents a viable way to ground world knowledge in embodied environments, it is still a trade-off rather than one best solution since we observe a considerable drop in correctness. Second, we focus on high-level to mid-level grounding, assuming there is a controller that can execute mid-level tasks (such as “grab cup”). Our work does not investigate the usefulness of LLMs for low-level sensorimotor behavior grounding. The third limitation is that we do not incorporate observation context or feedback into our models. To some extent, we approach LLMs in the same way as how VirtualHome asks human annotators to write action plans for a given human activity by imagination, in which case humans similarly do not observe environment context. However, we do see incorporating observation context for complex activities as an exciting future direction.
Despite the limitations, we are deeply encouraged by the promising findings that large language models (LLMs) contain rich actionable knowledge and that this knowledge can be appropriately extracted to plan actions for embodied agents when certain techniques are employed. We hope these findings can inspire future investigations into using pre-trained language models for goal-driven decision-making problems and grounding the learned knowledge in embodied environments.
Acknowledgment
--------------
We would like to thank OpenAI for providing academic access to the OpenAI API and Luke Metz for valuable feedback and discussions. This work was supported in part by Berkeley Deep Drive, NSF IIS-2024594, and GoodAI Research Award. |
19930e5d-23dc-4f22-acc5-380847ee1ed8 | trentmkelly/LessWrong-43k | LessWrong | Does scheming lead to adequate future empowerment? (Section 2.3.1.2 of "Scheming AIs")
This is Section 2.3.1.2 of my report “Scheming AIs: Will AIs fake alignment during training in order to get power?”. There’s also a summary of the full report here (audio here). The summary covers most of the main points and technical terms, and I’m hoping that it will provide much of the context necessary to understand individual sections of the report on their own.
Audio version of this section here, or search for "Joe Carlsmith Audio" on your podcast app.
Adequate future empowerment
So far in this analysis of the classic goal-guarding story, we've discussed whether to expect instrumental training-gaming to in fact guard the model's goals to the degree that the story requires. I think this is at least non-obvious – especially for more extreme variants of the goal-guarding hypothesis, on which the model's goals "crystallize" entirely after it starts training-gaming. Perhaps, though, empirical work can shed further light on the matter (see discussion in section 6.3 below).
For now, let's move to the other key component of the classic goal-guarding story – what I called "adequate future empowerment" above. Here, the question is: granted that training-gaming would guard the model's goals enough for it to be at least somewhat interested in empowering the future agents produced by training, will those agents in fact end up empowered to a degree that makes instrumental training-gaming a good strategy overall?
When is the "pay off" supposed to happen?
We're imagining, here, that the model is instrumentally training-gaming with some kind of "payoff" in mind – that is, some future point where the goals-it-supports will reach a position of sufficiently greater empowerment that it's worth training-gaming now in order to get them there. But we haven't yet said when, exactly, that future point is supposed to come. And we can distinguish between a number of different possibilities.
For example, we can imagine models that would be adequately satisfied if their goals merely |
35d1ec55-468f-4495-abba-18d51db0476a | LDJnr/LessWrong-Amplify-Instruct | LessWrong | "Imagine looking at your hand, and knowing nothing of cells, nothing of biochemistry, nothing of DNA. You’ve learned some anatomy from dissection, so you know your hand contains muscles; but you don’t know why muscles move instead of lying there like clay. Your hand is just . . . stuff . . . and for some reason it moves under your direction. Is this not magic?It seemed to me then, and it still seems to me, most probable that the animal body does not act as a thermodynamic engine . . . The influence of animal or vegetable life on matter is infinitely beyond the range of any scientific inquiry hitherto entered on. Its power of directing the motions of moving particles, in the demonstrated daily miracle of our human free-will, and in the growth of generation after generation of plants from a single seed, are infinitely different from any possible result of the fortuitous concourse of atoms[.]1[C]onsciousness teaches every individual that they are, to some extent, subject to the direction of his will. It appears, therefore, that animated creatures have the power of immediately applying, to certain moving particles of matter within their bodies, forces by which the motions of these particles are directed to produce desired mechanical effects.2Modern biologists are coming once more to a firm acceptance of something beyond mere gravitational, chemical, and physical forces; and that unknown thing is a vital principle.3—Lord KelvinThis was the theory of vitalism ; that the mysterious difference between living matter and non-living matter was explained by an Élan vital or vis vitalis. Élan vital infused living matter and caused it to move as consciously directed. Élan vital participated in chemical transformations which no mere non-living particles could undergo—Wöhler’s later synthesis of urea, a component of urine, was a major blow to the vitalistic theory because it showed that mere chemistry could duplicate a product of biology.Calling “Élan vital” an explanation, even a fake explanation like phlogiston, is probably giving it too much credit. It functioned primarily as a curiosity-stopper. You said “Why?” and the answer was “Élan vital!”When you say “Élan vital!” it feels like you know why your hand moves. You have a little causal diagram in your head that says:But actually you know nothing you didn’t know before. You don’t know, say, whether your hand will generate heat or absorb heat, unless you have observed the fact already; if not, you won’t be able to predict it in advance. Your curiosity feels sated, but it hasn’t been fed. Since you can say “Why? Élan vital!” to any possible observation, it is equally good at explaining all outcomes, a disguised hypothesis of maximum entropy, et cetera.But the greater lesson lies in the vitalists’ reverence for the Élan vital, their eagerness to pronounce it a mystery beyond all science. Meeting the great dragon Unknown, the vitalists did not draw their swords to do battle, but bowed their necks in submission. They took pride in their ignorance, made biology into a sacred mystery, and thereby became loath to relinquish their ignorance when evidence came knocking.The Secret of Life was infinitely beyond the reach of science! Not just a little beyond, mind you, but infinitely beyond! Lord Kelvin sure did get a tremendous emotional kick out of not knowing something.But ignorance exists in the map, not in the territory. If I am ignorant about a phenomenon, that is a fact about my own state of mind, not a fact about the phenomenon itself. A phenomenon can seem mysterious to some particular person. There are no phenomena which are mysterious of themselves. To worship a phenomenon because it seems so wonderfully mysterious is to worship your own ignorance.Vitalism shared with phlogiston the error of encapsulating the mystery as a substance. Fire was mysterious, and the phlogiston theory encapsulated the mystery in a mysterious substance called “phlogiston.” Life was a sacred mystery, and vitalism encapsulated the sacred mystery in a mysterious substance called “Élan vital.” Neither answer helped concentrate the model’s probability density—helped make some outcomes easier to explain than others. The “explanation” just wrapped up the question as a small, hard, opaque black ball.In a comedy written by Molière, a physician explains the power of a soporific by saying that it contains a “dormitive potency.” Same principle. It is a failure of human psychology that, faced with a mysterious phenomenon, we more readily postulate mysterious inherent substances than complex underlying processes.But the deeper failure is supposing that an answer can be mysterious. If a phenomenon feels mysterious, that is a fact about our state of knowledge, not a fact about the phenomenon itself. The vitalists saw a mysterious gap in their knowledge, and postulated a mysterious stuff that plugged the gap. In doing so, they mixed up the map with the territory. All confusion and bewilderment exist in the mind, not in encapsulated substances.This is the ultimate and fully general explanation for why, again and again in humanity’s history, people are shocked to discover that an incredibly mysterious question has a non-mysterious answer. Mystery is a property of questions, not answers.Therefore I call theories such as vitalism mysterious answers to mysterious questions.These are the signs of mysterious answers to mysterious questions:First, the explanation acts as a curiosity-stopper rather than an anticipation-controller.Second, the hypothesis has no moving parts—the model is not a specific complex mechanism, but a blankly solid substance or force. The mysterious substance or mysterious force may be said to be here or there, to cause this or that; but the reason why the mysterious force behaves thus is wrapped in a blank unity.Third, those who proffer the explanation cherish their ignorance; they speak proudly of how the phenomenon defeats ordinary science or is unlike merely mundane phenomena.Fourth, even after the answer is given, the phenomenon is still a mystery and possesses the same quality of wonderful inexplicability that it had at the start.1 Lord Kelvin, “On the Dissipation of Energy: Geology and General Physics,” in Popular Lectures and Addresses, vol. ii (London: Macmillan, 1894).2 Lord Kelvin, “On the Mechanical action of Heat or Light: On the Power of Animated Creatures over Matter: On the Sources available to Man for the production of Mechanical Effect,” Proceedings of the Royal Society of Edinburgh 3, no. 1 (1852): 108–113.3 Silvanus Phillips Thompson, The Life of Lord Kelvin (American Mathematical Society, 2005)."
A user from LessWrong is responsible for the text you see above
What is this text talking about?
This text is discussing the concept of "vitalism", a historical scientific theory that proposed a vital force or life force, separate from physical and chemical forces, was necessary to explain the processes of life. The text uses the example of a hand moving under one's own will, which to someone with no knowledge of cells, biochemistry, or DNA, might seem like a magical or unexplainable event. This mystery, the text argues, was often attributed to a vital force, or "Élan vital".
The author critiques this approach, arguing that it functions primarily as a "curiosity-stopper" rather than a true explanation. The concept of "Élan vital" is criticized as being too vague and non-specific, failing to predict or explain specific outcomes. The author also criticizes the tendency of vitalists to revere the mystery of life and resist scientific explanations.
The text further discusses the error of attributing mysterious phenomena to mysterious substances, like "phlogiston" for fire or "Élan vital" for life. It argues that mystery exists in our understanding, not in the phenomena themselves, and that proposing mysterious answers only perpetuates ignorance.
The author concludes by outlining the signs of such "mysterious answers to mysterious questions", which include acting as a curiosity-stopper, lacking specific mechanisms, cherishing ignorance, and leaving the phenomenon as mysterious as before. The text emphasizes that mystery is a property of questions, not answers, and that true explanations should reduce, not increase, the sense of mystery.
Elaborate on the concept of "curiosity-stopper". How does it differ from a true scientific explanation and why is it considered a hindrance to the progress of understanding?
A "curiosity-stopper" is a term used to describe an explanation that, rather than encouraging further inquiry and understanding, instead halts the process of questioning and exploration. It's a type of answer that might feel satisfying in the moment because it gives the illusion of understanding, but it doesn't actually increase our knowledge or understanding of the phenomenon in question.
In contrast, a true scientific explanation provides a detailed understanding of a phenomenon, based on empirical evidence and logical reasoning. It allows us to make predictions about the behavior of the phenomenon under different conditions, and it invites further questions and deeper understanding. It's an answer that leads to more questions, driving the cycle of scientific inquiry forward.
Curiosity-stoppers are considered a hindrance to the progress of understanding because they discourage further questioning and exploration. They provide a false sense of understanding that can prevent us from seeking out true, detailed, and useful explanations. By accepting a curiosity-stopper, we might miss out on the opportunity to discover more about the world and how it works.
For example, attributing a complex biological process to a vague concept like "Élan vital" might feel satisfying, but it doesn't actually tell us anything about the process itself. It doesn't help us predict what will happen under different conditions, and it doesn't invite further questions. It's a curiosity-stopper that hinders our understanding rather than promoting it.
How does the concept of "curiosity-stopper" apply to modern scientific debates and controversies?
The concept of "curiosity-stopper" can apply to modern scientific debates and controversies in several ways. It often surfaces when complex phenomena are explained away with overly simplistic or vague theories, halting further inquiry and investigation.
For example, in discussions about consciousness, some might argue that it's simply an emergent property of complex computation, without further detailing the mechanisms or processes involved. This could be seen as a curiosity-stopper because it doesn't provide a detailed understanding of consciousness or invite further questions.
In the realm of genetics, attributing certain traits or behaviors solely to "genes" without considering the intricate interplay of genetics, epigenetics, and environment can also be a curiosity-stopper. It simplifies a complex issue and potentially halts further exploration into how these factors interact.
In the context of climate change, some might argue that natural climate variability is the sole cause, ignoring the substantial evidence for human-induced climate change. This could be seen as a curiosity-stopper, as it discourages further investigation into the human activities contributing to climate change.
These examples demonstrate how curiosity-stoppers can hinder scientific progress by discouraging further questioning and exploration. They highlight the importance of maintaining a spirit of curiosity and skepticism in scientific inquiry, and the need for detailed, evidence-based explanations that invite further questions and deeper understanding. |
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