Research on AI systems’ behavior frequently focuses on predefined behavioral targets, such as sycophancy, deception, or reward hacking. While useful, it is unclear how far progress on individual targets translates into understanding (and later improving) models’ overall behavior.
In this post, I argue that two gaps make this difficult to assess: we lack a principled measure of how far findings on individual targets generalize, and recent work (Pawar et al., 2026; Liu et al., 2026) suggests that training on one value can affect others in ways that are hard to predict. I then review methods that do not require specifying targets beforehand, particularly model diffing, and propose directions I consider promising, drawing on my early pilot experiments.
Background
A common approach to studying AI systems’ behavior (Sharkey et al. 2023) is to focus on predefined behavioral targets, i.e., properties or patterns researchers define with respect to the models’ (context, output) pairs. They include desirable properties such as honesty, helpfulness, and harmlessness, and undesirable ones such as sycophancy, deception, and reward hacking.
However, this approach has several limitations. Chughtai, Engels and Nanda (2026) highlight one of them when motivating their experiments:
“Standard methods for assessing the safety and capabilities of frontier state-of-the-art LLMs rely on capability and propensity evaluations. This evaluation-driven paradigm has had reasonable success, but has a fundamental limitation - it can only expose things that you are looking for, which you know how to measure.”
I argue that being limited by the behaviors we can identify and specify beforehand does not necessarily undermine the usefulness of this approach, as long as progress on individual behavioral targets compounds into meaningful progress toward understanding and improving models' overall behavior. The question is whether this is actually the case.
Behavior, propensity and behavioral space
Before going further, I am using the following terms as defined by Sharkey et al. (2023):
Behavior: what a model outputs or does in a particular context, including its responses and actions
Propensity: a systematic tendency to exhibit a particular kind of behavior across a range of situations
Now, we can define what I refer to as behavioral space. I will use this term to refer to the set of possible (context, output) pairs, while keeping in mind that it is defined per model. Then, behavioral targets become properties that identify subsets of this space.
To make this idea more concrete, we can look at previous work that tried to better grasp the behavioral space by inspecting a wide range of (context, output) pairs observed "in the wild". Huang et al. (2025) identify over 3,000 values expressed by Claude in real-world conversations, while Anthropic's subsequent work (2026) organizes these values along four quantitative axes.
How far can progress on individual targets take us?
At the broadest level, we want AI models whose behavior is desirable overall. Because this goal is abstract, difficult to specify, and therefore difficult to evaluate directly, we often interpret model behavior through the lens of particular values and failure modes. This decomposition is useful and often necessary for current safety measures, because once we identify a value or failure mode, we can evaluate it, quantify it, investigate how it arises, and try to control it.
As previously mentioned, those studies are limited by our ability to specify what we want to look at. Even more, we don’t even know if we are identifying the right proxies for the targets we want to study. Gupta et al. (2026) warn that researchers may describe AI behavior as lying or scheming without enough evidence, especially when definitions are unclear, data are limited, or experiments fail to rule out other explanations. However, these limitations alone do not necessarily undermine the usefulness of this approach. Even if we cannot identify every relevant behavioral target beforehand, studying individual targets might still give us insights that help us understand and improve models' behavior more broadly.
The question is what needs to be true for this to happen. Here are my thoughts. These are not strict conditions, but rather considerations that could help us assess how far these methods can get us.
First, the values and failure modes we look at must either cover a meaningful portion of the relevant behavioral space or provide insights that help us understand and address behaviors beyond those we directly study. Coverage here is not simply about how many (context, output) pairs we study. Quantifying how much of that space these subsets cover requires specifying a measure. Different measures may give us very different notions of coverage, and it is not immediately clear which ones are most informative.
More importantly, even studying a small portion of the behavioral space could provide insights that generalize far beyond the behaviors we directly investigate. Conversely, studying a large number of behaviors does not necessarily imply that we are learning something about the model's behavior more broadly. We may also think we have changed a model’s broader propensity when we have only changed its responses in the situations we tested. My point is that, without a principled measure of coverage or an understanding of how far our insights generalize, we cannot easily determine how much progress studying individual targets actually produces.
Second, interventions on those components must combine in ways that support broader progress. If we want our efforts to compound, we need to understand how improvements on individual targets interact. However, we are not yet sure whether improving one desirable value may weaken another. Also, mitigating one failure mode may introduce or strengthen another.
My thoughts on this second point were mainly influenced by the work of Pawar et al. (2026), who show that training a model toward one value can affect other values and behaviors that were not directly targeted, and Liu et al. (2026), who find that cosine similarities between embeddings of value descriptions derived from Anthropic’s constitution are poor predictors of how training on one value affects others. In my view, these findings provide an interesting stress test of this second assumption.
Target-aware and target-agnostic methods
These limitations motivate a distinction between what I call target-aware and target-agnostic methods.
A target-aware method requires specifying a behavioral target before it can be applied.
A target-agnostic method can be applied without naming the target in advance.
It is important to distinguish between these two terms and the classification of methods as general. Basically, generality refers to whether the same method can be reused across different targets, while target awareness describes whether a target must be specified before applying the method.
One can see that a target-agnostic method is general by construction, as its application is, by definition, not tied to a particular behavioral target.
Evaluating specific model behavior: an intuitive example of a general method that is target-aware. Constructing a particular evaluation requires specifying the property to be measured so examples can be generated (Perez et al., 2023). Behavioral evaluations have investigated properties such as sycophancy (Sharma et al., 2023), metagaming (Schoen & Nitishinskaya, 2026), evaluation awareness (Needham et al., 2025), and dishonesty (Ren et al., 2025).
Inoculation prompting (Tan et al., 2025; Wichers et al., 2025): a method that adds an instruction mentioning the unwanted behavior within the fine-tuning prompts, e.g., when training on code that hard-codes answers to pass supplied tests, the added instruction explicitly asks for this shortcut. We classify inoculation as a target-aware, general modification method because it works across several kinds of unwanted behavior, but researchers must identify what to request.
Synthetic document fine-tuning (Greenblatt et al., 2024; Wang et al., 2025): another target-aware, general method that aims to make the model acquire a specified belief or association by training it on synthetic documents that treat the intended proposition as true.
Model Diffing
Model diffing offers a route to target-agnostic characterization by comparing models in ways that can surface differences (in model outputs or in internal representations) that were not specified beforehand.
Early work on white-box model diffing includes Lindsey et al. (2024), which use crosscoders, and Bricken et al. (2024), which use SAEs. These approaches use activation data to compare internal representations across models or training checkpoints. Bricken et al. also vary the data used for comparison to distinguish the effects of changing the inputs from those of changing the model.
An interesting case is Wang et al.'s (2025) white-box approach. They compare GPT-4o before and after fine-tuning on incorrect advice, using a sparse autoencoder (SAE) trained on activations from a fixed middle layer and kept unchanged. They rank features by activation increases on 44 evaluation questions, then add or subtract their decoder vectors to measure changes in replies expressing malicious intent or encouraging illegal or unethical actions. They find that one influential feature activates on speech by abusive characters; strengthening it makes the model respond similarly, hence the label "toxic persona". Repeating the comparison on fine-tuning examples instead of evaluation questions still places this feature and three sarcasm-related features among the top 100 changes. I view this as progress towards target-agnostic characterization. However, recognizing their significance and establishing an unexpected failure remain unresolved.
By comparison, Chen et al. (2025)begin with a specified behavior. They then prompt the model to display or avoid it and take the difference in average internal activations between the resulting response groups. This difference is their “persona vector.” They construct one vector per layer and select the layer where steering most strongly elicits the behavior, using the same coefficient across layers. The selected vector can then monitor or influence that behavior. Their procedure is reusable but target-aware: both constructing the vector and selecting the layer depend on knowing which behavior to measure.
The white-box methods above analyze hidden activations. In contrast, Aranguri and McGrath (2025) compare next-token logits before and after post-training. During generation, they amplify the difference between these logits and sample from the resulting distribution, effectively exaggerating the changes introduced by post-training. In their emergent-misalignment experiments, this makes harmful responses more frequent and therefore easier to detect. The amplification step does not require specifying a particular behavior beforehand, although the resulting samples still need investigation and evaluation. The point is to make behavioral changes easier to observe.
Text-only black-box model diffing instead compares generated responses without accessing the hidden activations or logits of the models being compared. For example, VibeCheck (Dunlap et al., 2025) asks an LLM to examine paired responses and propose qualitative axes along which they differ, such as tone or writing style. It then uses LLM judges to assess whether these discovered axes consistently distinguish the models, iteratively searching for additional differences that the existing axes fail to capture. Here, the focus is on discovering qualitative properties of responses, which need not concern misalignment to be relevant to understanding model behavior.
Chughtai, Engels, and Nanda (2026) extend this direction through model-diffing agents. Rather than analyzing responses from a fixed set of prompts, an auditor actively queries two models, proposes hypotheses about their differences, and chooses further prompts to test and refine them. Its task is to discover both what differs and under which conditions the difference appears. Their reported findings include differences in refusal behavior and in how models interpret code prompts. Allowing the auditor to adapt its queries also lets it investigate patterns that may not be clear from the initial examples. However, the investigation remains dependent on what the agent decides to explore and how it interprets the responses.
Some future directions
Looking at the prior work discussed above, two main patterns emerge:
Many of the methods discussed above compare two fixed models, typically before and after some intervention.
Neither target-agnostic nor target-aware comparisons necessarily reveal how the identified differences developed throughout training or how they interact with one another.
With these limitations laid out, we can see that existing approaches remain quite narrow in certain respects, which motivates exploring ways of studying model behavior that go beyond these patterns.
Studying behavioral development throughout training
Inspired by Bharadwaj and Kirk (2026), my view is that understanding incremental changes in behavior could help us build a more complete picture of model behavior as a whole.
With this in mind, one possible direction would be to compare models across intermediate post-training checkpoints using different methods, including target-aware evaluations and target-agnostic model diffing. A trend that appears under several methods is more credible, and a disagreement between them is itself worth investigating.
Additionally, organizing and standardizing experiments by model family, size, training stage, and checkpoint would be particularly insightful. In this setting, breadth could prove useful, because even without a principled measure of how much behavioral space we cover, studying many behavioral properties might reveal patterns and interactions we would otherwise miss.
In my own pilot experiments, I investigated several behavioral properties (e.g., reward gaming, sycophancy, evaluation awareness, and sandbagging) across released DPO and RL checkpoints of Ai2's OLMo 3.1 32B Think (DPO; RL steps 50, 1050, 2300) and OLMo 3 7B Think (DPO; RL steps 25, 625) models.
Looking at the broader "behavioral matrix", I found that measured levels of metric-seeking in reasoning, verbalized evaluation awareness, and sandbagging increased during RL in the 32B model, while reward gaming in final answers showed no clear trend under my initial judge. In comparison, none of these measures changed clearly across the evaluated 7B checkpoints, and my experiments on sycophancy showed no clear endpoint changes in either model.
Although the results were interesting, I also found some of them very sensitive to the choice of LLM judge, which highlighted to me the difficulty of reliably measuring behavioral changes, let alone explaining their causes.
The time dimension
Once we begin thinking about studies that range across checkpoints, there is an inherent new dimension that we get for free: time. While most current methods focus on static comparisons, leveraging this temporal dimension opens up new possibilities for assessing the significance of behavioral changes by allowing us to ask questions such as:
Could we measure how informative a discovered behavioral change is by investigating whether it helps predict other behaviors, or how those behaviors evolve throughout subsequent training?
Looking for warning signs
I am also interested in whether studying behavioral changes throughout training could help us identify early warning signs of undesirable behavior.
For example, we could investigate whether measures derived from black-box model diffing can identify checkpoints that warrant further investigation by examining whether spikes in these measures correspond to changes across our broader behavioral matrix.
Such signals would not necessarily indicate undesirable behavior, but could help us identify changes worth examining more closely.
In a related but distinct line of preliminary experiments, I explored whether disagreement between expressed reasoning and final answers could serve as such a warning sign. I fine-tuned Qwen3-14B and OLMo-3-7B-Think on incorrect health and legal advice from Wang et al. (2025), using answer-only training targets without reasoning traces.
With reasoning enabled during evaluation, Claude Sonnet 5.5 identified disagreements in 36–60% of eligible everyday responses across Qwen3-14B runs, and 29–73% across OLMo-3-7B-Think runs (roughly 30 judged responses per run), compared with none in matched correct-advice controls in the judged sample.
A separate harmless preference intervention on Qwen3-14B generally shifted reasoning and answers together.
However, I came to the conclusion that disagreement was not particularly useful as a warning sign, because broader behavioral changes were already visible in the final answers, while narrower changes often went unnoticed in both the reasoning and the answers. As such, looking at disagreement offered little additional insight over evaluating the final answers alone.
Conclusion
The discussion above identifies some important considerations for assessing how far progress on individual behavioral targets can take us.
Ultimately, answering this question depends on how we measure the significance of our findings beyond the behaviors we investigate. However, looking at previous work, I think we can argue that even developing an intuition for what such a measure should capture is particularly difficult in the study of model behavior.
Making progress on individual problems without having at least an intuition for how that progress contributes to our broader goal is, in my view, a concerning position to be in. This calls for a better understanding of model behavior and more creative approaches to studying it.
Acknowledgments
This work was conducted as part of the CAISH Alignment Desk, so I would like to thank the CAISH team for their valuable feedback.
Introduction
Research on AI systems’ behavior frequently focuses on predefined behavioral targets, such as sycophancy, deception, or reward hacking. While useful, it is unclear how far progress on individual targets translates into understanding (and later improving) models’ overall behavior.
In this post, I argue that two gaps make this difficult to assess: we lack a principled measure of how far findings on individual targets generalize, and recent work (Pawar et al., 2026; Liu et al., 2026) suggests that training on one value can affect others in ways that are hard to predict. I then review methods that do not require specifying targets beforehand, particularly model diffing, and propose directions I consider promising, drawing on my early pilot experiments.
Background
A common approach to studying AI systems’ behavior (Sharkey et al. 2023) is to focus on predefined behavioral targets, i.e., properties or patterns researchers define with respect to the models’ (context, output) pairs. They include desirable properties such as honesty, helpfulness, and harmlessness, and undesirable ones such as sycophancy, deception, and reward hacking.
However, this approach has several limitations. Chughtai, Engels and Nanda (2026) highlight one of them when motivating their experiments:
I argue that being limited by the behaviors we can identify and specify beforehand does not necessarily undermine the usefulness of this approach, as long as progress on individual behavioral targets compounds into meaningful progress toward understanding and improving models' overall behavior. The question is whether this is actually the case.
Behavior, propensity and behavioral space
Before going further, I am using the following terms as defined by Sharkey et al. (2023):
Now, we can define what I refer to as behavioral space. I will use this term to refer to the set of possible (context, output) pairs, while keeping in mind that it is defined per model. Then, behavioral targets become properties that identify subsets of this space.
To make this idea more concrete, we can look at previous work that tried to better grasp the behavioral space by inspecting a wide range of (context, output) pairs observed "in the wild". Huang et al. (2025) identify over 3,000 values expressed by Claude in real-world conversations, while Anthropic's subsequent work (2026) organizes these values along four quantitative axes.
How far can progress on individual targets take us?
At the broadest level, we want AI models whose behavior is desirable overall. Because this goal is abstract, difficult to specify, and therefore difficult to evaluate directly, we often interpret model behavior through the lens of particular values and failure modes. This decomposition is useful and often necessary for current safety measures, because once we identify a value or failure mode, we can evaluate it, quantify it, investigate how it arises, and try to control it.
As previously mentioned, those studies are limited by our ability to specify what we want to look at. Even more, we don’t even know if we are identifying the right proxies for the targets we want to study. Gupta et al. (2026) warn that researchers may describe AI behavior as lying or scheming without enough evidence, especially when definitions are unclear, data are limited, or experiments fail to rule out other explanations. However, these limitations alone do not necessarily undermine the usefulness of this approach. Even if we cannot identify every relevant behavioral target beforehand, studying individual targets might still give us insights that help us understand and improve models' behavior more broadly.
The question is what needs to be true for this to happen. Here are my thoughts. These are not strict conditions, but rather considerations that could help us assess how far these methods can get us.
First, the values and failure modes we look at must either cover a meaningful portion of the relevant behavioral space or provide insights that help us understand and address behaviors beyond those we directly study. Coverage here is not simply about how many (context, output) pairs we study. Quantifying how much of that space these subsets cover requires specifying a measure. Different measures may give us very different notions of coverage, and it is not immediately clear which ones are most informative.
More importantly, even studying a small portion of the behavioral space could provide insights that generalize far beyond the behaviors we directly investigate. Conversely, studying a large number of behaviors does not necessarily imply that we are learning something about the model's behavior more broadly. We may also think we have changed a model’s broader propensity when we have only changed its responses in the situations we tested. My point is that, without a principled measure of coverage or an understanding of how far our insights generalize, we cannot easily determine how much progress studying individual targets actually produces.
Second, interventions on those components must combine in ways that support broader progress. If we want our efforts to compound, we need to understand how improvements on individual targets interact. However, we are not yet sure whether improving one desirable value may weaken another. Also, mitigating one failure mode may introduce or strengthen another.
My thoughts on this second point were mainly influenced by the work of Pawar et al. (2026), who show that training a model toward one value can affect other values and behaviors that were not directly targeted, and Liu et al. (2026), who find that cosine similarities between embeddings of value descriptions derived from Anthropic’s constitution are poor predictors of how training on one value affects others. In my view, these findings provide an interesting stress test of this second assumption.
Target-aware and target-agnostic methods
These limitations motivate a distinction between what I call target-aware and target-agnostic methods.
It is important to distinguish between these two terms and the classification of methods as general. Basically, generality refers to whether the same method can be reused across different targets, while target awareness describes whether a target must be specified before applying the method.
One can see that a target-agnostic method is general by construction, as its application is, by definition, not tied to a particular behavioral target.
General
Not General
Target-aware
LLM-as-a-judge evaluation (with targets specified beforehand)
Specific alignment-faking experiment (Greenblatt et al., 2024)
Target-agnostic
Agent-based black-box model diffing
-
To offer some examples:
Model Diffing
Model diffing offers a route to target-agnostic characterization by comparing models in ways that can surface differences (in model outputs or in internal representations) that were not specified beforehand.
Early work on white-box model diffing includes Lindsey et al. (2024), which use crosscoders, and Bricken et al. (2024), which use SAEs. These approaches use activation data to compare internal representations across models or training checkpoints. Bricken et al. also vary the data used for comparison to distinguish the effects of changing the inputs from those of changing the model.
An interesting case is Wang et al.'s (2025) white-box approach. They compare GPT-4o before and after fine-tuning on incorrect advice, using a sparse autoencoder (SAE) trained on activations from a fixed middle layer and kept unchanged. They rank features by activation increases on 44 evaluation questions, then add or subtract their decoder vectors to measure changes in replies expressing malicious intent or encouraging illegal or unethical actions. They find that one influential feature activates on speech by abusive characters; strengthening it makes the model respond similarly, hence the label "toxic persona". Repeating the comparison on fine-tuning examples instead of evaluation questions still places this feature and three sarcasm-related features among the top 100 changes. I view this as progress towards target-agnostic characterization. However, recognizing their significance and establishing an unexpected failure remain unresolved.
By comparison, Chen et al. (2025) begin with a specified behavior. They then prompt the model to display or avoid it and take the difference in average internal activations between the resulting response groups. This difference is their “persona vector.” They construct one vector per layer and select the layer where steering most strongly elicits the behavior, using the same coefficient across layers. The selected vector can then monitor or influence that behavior. Their procedure is reusable but target-aware: both constructing the vector and selecting the layer depend on knowing which behavior to measure.
The white-box methods above analyze hidden activations. In contrast, Aranguri and McGrath (2025) compare next-token logits before and after post-training. During generation, they amplify the difference between these logits and sample from the resulting distribution, effectively exaggerating the changes introduced by post-training. In their emergent-misalignment experiments, this makes harmful responses more frequent and therefore easier to detect. The amplification step does not require specifying a particular behavior beforehand, although the resulting samples still need investigation and evaluation. The point is to make behavioral changes easier to observe.
Text-only black-box model diffing instead compares generated responses without accessing the hidden activations or logits of the models being compared. For example, VibeCheck (Dunlap et al., 2025) asks an LLM to examine paired responses and propose qualitative axes along which they differ, such as tone or writing style. It then uses LLM judges to assess whether these discovered axes consistently distinguish the models, iteratively searching for additional differences that the existing axes fail to capture. Here, the focus is on discovering qualitative properties of responses, which need not concern misalignment to be relevant to understanding model behavior.
Chughtai, Engels, and Nanda (2026) extend this direction through model-diffing agents. Rather than analyzing responses from a fixed set of prompts, an auditor actively queries two models, proposes hypotheses about their differences, and chooses further prompts to test and refine them. Its task is to discover both what differs and under which conditions the difference appears. Their reported findings include differences in refusal behavior and in how models interpret code prompts. Allowing the auditor to adapt its queries also lets it investigate patterns that may not be clear from the initial examples. However, the investigation remains dependent on what the agent decides to explore and how it interprets the responses.
Some future directions
Looking at the prior work discussed above, two main patterns emerge:
With these limitations laid out, we can see that existing approaches remain quite narrow in certain respects, which motivates exploring ways of studying model behavior that go beyond these patterns.
Studying behavioral development throughout training
Inspired by Bharadwaj and Kirk (2026), my view is that understanding incremental changes in behavior could help us build a more complete picture of model behavior as a whole.
With this in mind, one possible direction would be to compare models across intermediate post-training checkpoints using different methods, including target-aware evaluations and target-agnostic model diffing. A trend that appears under several methods is more credible, and a disagreement between them is itself worth investigating.
Additionally, organizing and standardizing experiments by model family, size, training stage, and checkpoint would be particularly insightful. In this setting, breadth could prove useful, because even without a principled measure of how much behavioral space we cover, studying many behavioral properties might reveal patterns and interactions we would otherwise miss.
In my own pilot experiments, I investigated several behavioral properties (e.g., reward gaming, sycophancy, evaluation awareness, and sandbagging) across released DPO and RL checkpoints of Ai2's OLMo 3.1 32B Think (DPO; RL steps 50, 1050, 2300) and OLMo 3 7B Think (DPO; RL steps 25, 625) models.
Looking at the broader "behavioral matrix", I found that measured levels of metric-seeking in reasoning, verbalized evaluation awareness, and sandbagging increased during RL in the 32B model, while reward gaming in final answers showed no clear trend under my initial judge. In comparison, none of these measures changed clearly across the evaluated 7B checkpoints, and my experiments on sycophancy showed no clear endpoint changes in either model.
Although the results were interesting, I also found some of them very sensitive to the choice of LLM judge, which highlighted to me the difficulty of reliably measuring behavioral changes, let alone explaining their causes.
The time dimension
Once we begin thinking about studies that range across checkpoints, there is an inherent new dimension that we get for free: time. While most current methods focus on static comparisons, leveraging this temporal dimension opens up new possibilities for assessing the significance of behavioral changes by allowing us to ask questions such as:
Could we measure how informative a discovered behavioral change is by investigating whether it helps predict other behaviors, or how those behaviors evolve throughout subsequent training?
Looking for warning signs
I am also interested in whether studying behavioral changes throughout training could help us identify early warning signs of undesirable behavior.
For example, we could investigate whether measures derived from black-box model diffing can identify checkpoints that warrant further investigation by examining whether spikes in these measures correspond to changes across our broader behavioral matrix.
Such signals would not necessarily indicate undesirable behavior, but could help us identify changes worth examining more closely.
In a related but distinct line of preliminary experiments, I explored whether disagreement between expressed reasoning and final answers could serve as such a warning sign. I fine-tuned Qwen3-14B and OLMo-3-7B-Think on incorrect health and legal advice from Wang et al. (2025), using answer-only training targets without reasoning traces.
With reasoning enabled during evaluation, Claude Sonnet 5.5 identified disagreements in 36–60% of eligible everyday responses across Qwen3-14B runs, and 29–73% across OLMo-3-7B-Think runs (roughly 30 judged responses per run), compared with none in matched correct-advice controls in the judged sample.
A separate harmless preference intervention on Qwen3-14B generally shifted reasoning and answers together.
However, I came to the conclusion that disagreement was not particularly useful as a warning sign, because broader behavioral changes were already visible in the final answers, while narrower changes often went unnoticed in both the reasoning and the answers. As such, looking at disagreement offered little additional insight over evaluating the final answers alone.
Conclusion
The discussion above identifies some important considerations for assessing how far progress on individual behavioral targets can take us.
Ultimately, answering this question depends on how we measure the significance of our findings beyond the behaviors we investigate. However, looking at previous work, I think we can argue that even developing an intuition for what such a measure should capture is particularly difficult in the study of model behavior.
Making progress on individual problems without having at least an intuition for how that progress contributes to our broader goal is, in my view, a concerning position to be in. This calls for a better understanding of model behavior and more creative approaches to studying it.
Acknowledgments
This work was conducted as part of the CAISH Alignment Desk, so I would like to thank the CAISH team for their valuable feedback.