It doesn't seem like a huge deal to depend on the existence of smaller LLMs - they'll be cheap compared to the bigger one, and many LM series already contain smaller models. Not transferring between sites seems like a problem for any kind of reconstruction based metric because there's actually just differently important information in different parts of the model.

Sorry I meant the Anthropiclike neuron resampling procedure.

I think I misread Neel's comment, I thought he was saying that 131k was chosen because larger autoencoders would have too many dead latents (as opposed to this only being for Pythia residual).

Another question: any particular reason to expect ablate-to-zero to be the most relevant baseline? In my experiments, I find ablate to zero to completely destroy the loss. So it's unclear whether 90% recovered on this metric actually means that much - GPT-2 probably recovers 90% of the loss of GPT-4 under this metric, but obviously GPT-2 only explains a tiny fraction of GPT-4's capabilities. I feel like a more natural measure may be for example the equivalent compute efficiency hit.

Got it - do you think with a bit more tuning the feature death at larger scale could be eliminated, or would it be tough to manage with the reinitialization approach?

Makes sense that the shift would be helpful

Thanks, that makes sense

Great paper! The gating approach is an interesting way to learn the JumpReLU threshold and it's exciting that it works well. We've been working on some related directions at OpenAI based on similar intuitions about feature shrinking.

Some questions:

• Is b_mag still necessary in the gated autoencoder?
• Did you sweep learning rates for the baseline and your approach?
• How large is the dictionary of the autoencoder?

For your dashboards, how many tokens are you retrieving the top examples from?

Why do you scale your MSE by 1/(x_centred**2).sum(dim=-1, keepdim=True).sqrt() ? In particular, I'm confused about why you have the square root. Shouldn't it just be 1/(x_centred**2).sum(dim=-1, keepdim=True)?

I think this paper is empirical evidence for a nontrivial part of the deceptive alignment argument (RLHF/adversarial training being insufficient to remove it), and I also think most empirical papers don't make any sense when applied to AGI.

I think I have an intellectually consistent stance - I don't think this is because I have a double standard for pessimistic results.

First, suppose you did an experiment where you show models that usually kick puppies and hide a sleeper agent that suddenly becomes helpful and harmless in 2024, and adversarial training failing to remove this. I think I would draw the exact same conclusion about deceptive alignment from this experiment where the labels are painted on differently but the mechanics are the same. And just as I think it is invalid to conclude from the sleeper agent paper that models naturally want to insert backdoors in code even if they're harmless now, it is also invalid to argue from this hypothetical experiment that models naturally want to be helpful even if you try to train them to kick puppies.

Second, I think this paper is actually genuinely better evidence for deceptive alignment than many of the "deception" papers that came before. For example, I claim that the sycophancy and insider trading papers provide approximately no evidence for deceptive alignment. This is for exactly the same reason why I think showing RLHF making models harmless provides approximately no evidence against deceptive alignment. So I don't think it's true that I like empirical papers as long as they purport to support the deceptive alignment argument.

The reasons I think this paper is actually better than the other deception papers (beyond just quality of execution) are that the deceptive alignment in this setup happens for reasons more similar to why it might happen in AGI than in previous work, and the secret scratchpad setting seeming more analogous to AGI than single shot or visible scratchpad.