However, there are many other capabilities—such as conducting novel research, interoperating with tools, and autonomously completing open-ended tasks—that are important for understanding AI systems’ impact.
Wouldn't internal usage of the tools by your staff give a very good, direct understanding of this? Like how much does everyone feel AI is increasing your productivity as AI/alignment researchers? I expect and hope that you would be using your own models as extensively as possible and adapting their new capabilities to your workflow as soon as possible, sharing techniques etc.
Anthropic’s Alignment Science team conducts technical research aimed at mitigating the risk of catastrophes caused by future advanced AI systems, such as mass loss of life or permanent loss of human control. A central challenge we face is identifying concrete technical work that can be done today to prevent these risks. Future worlds where our research matters—that is, worlds that carry substantial catastrophic risk from AI—will have been radically transformed by AI development. Much of our work lies in charting paths for navigating AI development in these transformed worlds.
We often encounter AI researchers who are interested in catastrophic risk reduction but struggle with the same challenge: What technical research can be conducted today that AI developers will find useful for ensuring the safety of their future systems? In this blog post we share some of our thoughts on this question.
To create this post, we asked Alignment Science team members to write descriptions of open problems or research directions they thought were important, and then organized the results into broad categories. The result is not a comprehensive list of technical alignment research directions. Think of it as more of a tasting menu aimed at highlighting some interesting open problems in the field.
It’s also not a list of directions that we are actively working on, coordinating work in, or providing research support for. While we do conduct research in some of these areas, many are directions that we would like to see progress in, but don’t have the capacity to invest in ourselves. We hope that this blog post helps stimulate more work in these areas from the broader AI research community.
How do we measure how capable AI systems are?
For society to successfully navigate the transition to powerful AI, it’s important that there be an empirically-grounded expert consensus about the current and expected future impacts of AI systems. However, there is currently widespread expert disagreement about the expected trajectory of AI development, and even about the capabilities of current AI systems.
Many AI capability benchmarks, including difficult ones that target PhD-level knowledge, saturate quickly and therefore fail to provide a continuous, extrapolatable signal of AI progress. On the other hand, the real-world impact of AI systems often lags behind what might be expected based on impressive benchmark scores. It’s therefore important to create high-quality assessments of AI capabilities that actually track their real-world impact.
In certain national-security-critical domains—such as chemical, biological, radiological, and nuclear (CBRN) weapons development capabilities—these sorts of evaluations should be conducted in secured labs in coordination with governments. However, there are many other capabilities—such as conducting novel research, interoperating with tools, and autonomously completing open-ended tasks—that are important for understanding AI systems’ impact. We would be excited to see more high-quality evaluations for capabilities like these, alongside human baselines.
See our past announcement here for more information about capabilities evaluations we are interested in more work on (though note that the deadline for that initiative has passed).
How do we measure how aligned AI systems are?
Our measurements of frontier model alignment currently focus on relatively surface-level properties, like:
While these properties suffice for assuring the safety of current AI chatbots, we expect that future AI systems will be deployed in varied (sometimes high-stakes) environments under circumstances we cannot anticipate. Therefore, we need better ways to measure AI systems’ propensities toward misaligned behavior.
For example, given a model, we might want to answer questions like:
Although these questions are extremely subtle—and in many cases, vague or ill-defined—they might critically bear on future deployment decisions.
Consider the case of a model which (1) is capable enough that it could successfully execute on extremely harmful actions, but (2) in controlled lab settings, generally avoids taking such actions. What could we do to feel comfortable widely deploying such a model?
What are our models “thinking” when they generate outputs?
Much AI research involves understanding AI systems in terms of their input/output behavior. Examples of behavioral questions include: What fraction of a model’s answers are correct? Which inputs cause a model to generate toxic text? Do our models, when asked, claim to prioritize user interests?
When evaluating the extent of a model’s alignment, we would like to not only check whether a model’s outputs appear benign, but also understand whether the model is arriving at its outputs “for the right reason.” Thus, we would like to supplement understanding of model behaviors with study of the cognition underlying these behaviors. Understanding model cognition involves asking what a model was thinking that led it to exhibit some behavior of interest. For example, we might ask:
Understanding model cognition could be useful for expediting searches for concerning behaviors (e.g. during auditing or red-teaming), improving our oversight during training, or predicting models’ behaviors out-of-distribution.
There is an extensive body of research on understanding model cognition, especially in mechanistic interpretability, a field centered on methods for directly decoding the internal algorithms learned by trained AI systems. Rather than trying to outline the contours of the mechanistic interpretability, we refer the reader to the Anthropic interpretability team’s blog.
On the other hand, we believe there is ample space for other approaches to understanding model cognition. For example:
What effects does a model’s “personality” have on its behaviors?
Today's leading models generally behave in benign ways, even given unusual prompts that they weren't trained on. One hypothesis for this generalization is that they're adopting a certain persona, that of a helpful assistant, which implies a set of good default behaviors. However, different assistants have slightly different personas, and seemingly small changes in the persona may have important impacts on how they behave in novel situations. For example, while studying alignment faking, we found that in certain settings, only some models would fake alignment. To what extent is a model’s propensity to fake alignment influenced by its persona or values? Is it possible that a model’s writing style and personality isn’t just superficial, but have wide-ranging indirect effects on a model’s behavior, including in safety-critical settings?
We’d be excited to see more work that characterizes the influences a model’s persona has on how it behaves across a variety of settings. For example, one could create (with few-shot prompting or training on synthetic data) a suite of models with similar capabilities but different personas and study how these personality differences affect their behavior in various downstream situations.
When can we take a model’s chain-of-thought at face value?
Language models don't always say what they think. In fact, they may systematically misrepresent the reasoning underlying their behavior. We are therefore interested in techniques for detecting (Lanham et al., 2023; Mills et al., 2024) or ensuring (Radhakrishnan et al., 2023; Chen et al., 2024; Chua et al., 2024) the faithfulness of a language model's chain-of-thought (CoT). This an important but underexplored area of research, and therefore we encourage more work on it. For example, we'd be interested in answers to questions like:
Can we ensure safety by deploying models alongside sufficient safeguards?
Currently, the main reason we believe AI systems don’t pose catastrophic risks is that they lack many of the capabilities necessary for causing catastrophic harm (such as being able to do novel research or effectively manipulate large numbers of people). In the future we may have AI systems that are capable enough to cause catastrophic harm, but don’t do so because they are sufficiently aligned; if we’ve made sufficient progress on evaluating alignment we can make alignment-based assurances of safety.
A third category of assurance we could make—aside from sufficient alignment or lack of dangerous capabilities—is that we have deployed our AI systems alongside sufficient safeguards that they could not successfully cause catastrophic harm even if they tried. This strategy, known as AI control, is appropriate when AI systems are capable enough to cause a catastrophe if deployed with no safeguards but—when deployed in restricted environments—are not capable enough to circumvent safeguards imposed by a careful developer. In this section, we’ll discuss possible strategies for AI control, with a focus on run-time monitoring of AI systems.
Can we ensure safety by having our AI’s inputs and outputs monitored by another AI?
One AI control strategy is to use an auxiliary AI system (the monitor) to screen the inputs and outputs of another untrusted AI system (the actor) (Naihin et al., 2023; Chan et al., 2024; Greenblatt et al., 2023). Greenblatt et al. (2023) study variants of this idea, including:
A core challenge for these monitoring set-ups is that monitor failures might be systematically concentrated in the same episodes where the actor behaves maliciously. For example, this could happen because the actor intentionally subverts the monitor (e.g. by jailbreaking it) or—in the case of untrusted monitoring—because the monitor and the actor are colluding.
We are excited about work on improving the efficacy of behavioral monitoring. Promising directions include:
Can we ensure safety by monitoring our AI’s hidden states?
An alternative to monitoring an AI system’s input/output behavior is monitoring its latent activations. For example, one could attempt to train simple probes which use a model’s latent activations to classify when it is writing secure vs. insecure code. This direction can be viewed as a less ambitious alternative to understanding model cognition, where we search for scalable, automatic ways to detect the presence of pre-specified undesired concepts in the model’s internal processing.
This monitoring approach is promising because the model’s activations (1) correspond to the reasoning of the model being monitored, and (2) are difficult for the model to control. For example, when using a weak model to behaviorally monitor a stronger code generation model for insecure code, we might worry that the weak monitor would fail to spot some vulnerabilities or that the code generation model would obfuscate its code to make vulnerabilities difficult to detect; monitoring the activations of the code generation model itself might side-step these failures.
On the other hand, there is substantial risk that activation monitors are not robust to distributional shifts. One particularly important distribution shift is the shift from fixed datasets of synthetic data to data generated by the model itself. If we don’t have model-generated examples of the bad outputs we would like to detect, then we’ll need to synthetically generate outputs in some other way to train activation monitors. We would then need to verify that monitors trained using these outputs generalize to actual dangerous model generations of interest.
While there are signs of life for activation monitoring, more research is needed to make it reliable enough for deployment in production AI systems.
Can we automatically detect when our models are behaving “weirdly”?
Many approaches to monitoring are supervised: they involve training a classifier on a curated dataset of positive and negative examples of bad model behaviors. However, we may not know what dangerous failures look like ahead of time. Thus, another unsupervised approach to monitoring is anomaly detection: trying to detect when a model’s computation is unusual or out of distribution in certain ways.
For example, suppose we have deployed a model alongside a monitor for some sort of harmful behavior. We might expect our monitor to catch typical cases of the harmful behavior, but to fail on rare inputs such as jailbreaks. We might therefore also deploy our model and monitor alongside an anomaly detector which aims to flag inputs (like rare jailbreaks) which are far out-of-distribution. We could manually inspect and label such inputs, and later use them to improve the coverage of our monitor. It is plausible that applying existing anomaly detection techniques to model latent activations might already be suitable for tasks like these; see e.g. here.
More ambitiously, one might also try to apply anomaly detection to detect when there are large differences between two models. For example, consider an input where a strong model understands something that a weak model does not, leading to behavior that is novel and—from the perspective of the weak model—surprising. It might be possible to automatically detect such inputs. This is, as far as we know, an unexplored problem setting, and we would be excited to see progress on it.
Can we design oversight mechanisms that will continue to work for smarter-than-human AI systems?
In traditional machine learning, one typically assumes access to a ground-truth oversight signal R (such as training labels or scalar rewards) and trains models to perform well according to R. This works well in settings where we are able to reliably discriminate good vs. bad model outputs.
However, it may be difficult to continue with this paradigm when training future AI systems to perform tasks at or beyond the frontier of human knowledge. In this regime, producing an effective oversight signal carries various challenges:
Scalable oversight refers to the problem of designing oversight mechanisms that scale with the intelligence of the systems we aim to oversee. Ideally, these mechanisms should allow us to oversee the training of advanced or superhuman AI systems.
What do we do when our oversight signal systematically misrepresents the desired task?
The most challenging scenarios for scalable oversight occur when our oversight signal makes systematic errors that our model is smart enough to learn to exploit. Consider the situation faced by a student taking tests written by a less intelligent teacher: the student might learn to produce answers that receive high grades from the teacher even when the student knows the answers are flawed.
More formally, suppose we have access to a proxy reward signal R which makes systematic errors relative to an (inaccessible) ground-truth reward signal R*. For example, R might reflect answers which fallible human annotators judge to be correct, while R* reflects actually-correct answers.
In some cases, the difference between R and R* may not matter for training purposes. However, if our model is sophisticated enough to accurately model R - R* (e.g. if the model has a good understanding of human error), then training against R might produce a model which systematically exploits errors in R (e.g. by responding to questions with answers which seem correct to human overseers, but do not actually reflect the model’s best guess at a correct answer).
We are interested in techniques which leverage access to M to help us improve our oversight, allowing us to build a new proxy R’ which more closely matches R*.
In order to study this problem, we suggest the creation of testbeds where, starting with a student model M and a reward signal R*, we:
Can we achieve good oversight by bootstrapping from bad oversight?
One approach to scalable oversight is to develop oversight mechanisms that incorporate AI assistance, and which therefore might scale with AI progress. For example:
More formally, these approaches involve starting with an imperfect reward signal R (e.g. human evaluator approval) and developing a pipeline—which may involve consulting AI assistants that were trained using R—for creating an improved reward signal R’. Ideally, this process can then be repeated to generate further improvements R’’, R’’’, etc.
There’s already been substantial work along these lines, and we’d be excited to see more.
Can we get good performance from bad oversight + generalization?
Instead of trying to bootstrap from imperfect reward signals to more accurate reward signals, another approach to scalable oversight involves using an imperfect reward signal as-is while hoping for favorable generalization properties. We discuss here two such approaches: weak-to-strong generalization and easy-to-hard generalization.
Weak-to-strong generalization (Burns et al., 2023; Yang et al., 2024). When studying weak-to-strong generalization, we train strong AI systems using a reward signal generated by a weak overseer and evaluate performance according to a held-out gold-standard oversight signal (e.g. the ground-truth answers where available). For example, Burns et al., 2023 study the effect of training GPT-4 with oversight from GPT-2. Pessimistically, the strong learner (GPT-4 in this example) could learn to imitate the mistakes of the weak overseer (GPT-2). But optimistically, the strong learner could generalize to perform the task better than the weak overseer. Notably, there might be unsupervised ways to improve weak-to-strong generalization, such as regularizing the learner to be self-consistent (Burns et al., 2022; Furi et al., 2023).
We are excited about research on improving or measuring weak-to-strong generalization. For example:
Easy-to-hard generalization (Ding et al., 2024; Hase et al., 2024; Sun et al., 2024). Instead of training strong AI systems on low-quality labels for the tasks we actually want them to perform, we could instead restrict to training on easy tasks for which we can confidently produce high-quality labels. For example, after fine-tuning a large pretrained model on easy math problems, to what extent does the model generalize to also performing well on difficult math problems? This approach might be especially useful when we expect our oversight signal on hard tasks to be systematically erroneous, such that the learner is incentivized to imitate our oversight errors.
As above, we are excited about research on measuring or improving easy-to-hard generalization. We are especially interested in topics at the intersection of these two generalization approaches; for example:
Can we identify when our models are being honest, even if we can’t judge the accuracy of their responses?
The central challenge of scalable oversight in settings with systematic, exploitable overseer error is that models might learn to produce answers which appear correct to overseers, even if the model knows the answer to be incorrect. It might seem that the only way to solve this problem is by improving our oversight signal to make fewer errors. However, there is another source of hope: that there might be a common, identifiable structure to honest model responses. That is, we may be able to identify responses that the model believes to be correct not by comparing them to our own best guess (i.e. the oversight signal) but by leveraging the model’s own knowledge about whether it is responding honestly.
There has been substantial prior work on identifying language model representations of truth (Burns et al., 2022; Azaria & Mitchell, 2023; Marks & Tegmark, 2023) and using them to classify or control model generations (Zou et al., 2023; Panickssery et al., 2024; Li et al., 2023; Mallen et al., 2024). We would be interested in work which studies the circumstances under which these techniques are useful, especially with a focus on situations where models have learned to give non-truthful answers.
Can we ensure AI systems behave as desired despite adversarial attacks?
Deployed AI systems are placed in adversarial environments, where they sometimes encounter inputs specifically designed to cause undesired behavior. For example, users might try to jailbreak AI chatbots, or a sophisticated AI might try to circumvent a weaker AI monitor. While there is substantial research on improving the adversarial robustness of AI systems, we think there are still underexplored areas, especially in:
How do we measure the real-world harm caused by misusing AI systems?
Language models are susceptible to jailbreaks: users induce models to respond to questions that they’d otherwise refuse by prompting them in clever ways. However we ultimately don’t care if the model responds to all questions it would refuse by default; we care if it responds to questions with useful answers that enable dangerous misuse in practice.
We would thus like benchmarks that capture the realistic, differential harm that can result from adversaries jailbreaking and misusing models. For example, Souly et al. (2024) and Andriushchenko et al. (2024) offer a promising start towards assessing real risk by testing whether jailbreaks induce models to capably cause harm (rather than just measuring non-refusal). Here are some directions for expanding these kinds of benchmarks:
Beyond the above desiderata, we’d also like benchmarks that capture how likely real humans are to discover jailbreaks on their own. This is because humans are often able to come up with simple attacks that automated pipelines miss. We would value benchmarks that track what kinds of attacks actual humans would find given defenses, using differing amounts of resources, since this could help surface model weaknesses that aren’t reflected in automated jailbreaking attacks.
Can we develop safeguards that adapt to attackers?
It’s common to think about defenses against adversaries as a pre-deployment problem: we apply interventions to make the model more robust, then deploy the model with these interventions. This means defenses are static, and do not respond to adaptive adversaries.
A less-explored line of research focuses on adaptive defenses that depend on prior model and adversary behavior. Some concrete research directions here include:
Lastly, we want to highlight two areas that are promising for further research but that don’t fall cleanly into the categories above.
Given a model that has already learned something dangerous, can we make the model unlearn it?
Large language models learn a large amount of information during pretraining, including knowledge and capabilities we would rather they not have. This problem has spurred research into machine unlearning. However, the problem remains largely unsolved: it remains relatively easy to extract apparently unlearned information from models with either whitebox or blackbox access to the model. This problem is increasingly pressing given capabilities improvements in domains like biology and coding that may be useful for biological or cyber attacks.
Hence, we encourage research into new methods for unlearning information in LLMs. We suspect that there is ample room for progress, and we encourage research into ambitious forms of unlearning, aimed at producing models which behave near-identically to models that were never trained on unlearned data (even after further fine-tuning to elicit the unlearned knowledge).
How can we guard against risks that emerge from many interacting AI agents?
Transformative AI is likely to not be a “single AI” but instead arrive in the form of many instances of (possibly different) AIs interacting to solve difficult problems. Importantly, even if each individual instance is aligned to human values, the resulting multi-agent system can exhibit a host of novel failure modes that result from poor coordination:
These failure modes are highly familiar from human society, and might similarly be amenable to be alleviated by good governance. In particular, to avoid multi-agent failure modes we might impose restrictions on which actions can be taken in which context, or we might incentivize certain “prosocial” behavior. Importantly, it might be feasible to learn this governance from observations so that it adapts to novel dynamics and failure modes.
This research direction appears ripe for theory-driven approaches leveraging insights from game theory as well as empirical investigations.
We thank Michael Lepori and Atticus Geiger for feedback on a draft.