thoughts on what to work on in a world with heavy AI automation

it seems undeniable at this point that AI automation will play a huge role in all research in the medium term future. therefore, we should take automation into account when choosing what to work on. here are some possibilities, in decreasing order of how optimistic you are that models will be good at alignment research.

• push for people to allocate more resources to alignment. the most optimistic assumption is that models are perfect drop in replacements for human researchers, and are equally good as good at alignment and capabilities research as humans are. then, we just need to allocate more compute to alignment and we're chilling. the main problem is there is an incentive to race to the bottom, to allocate more to capabilities to have a faster recursive improvement loop. but it is much easier to legislate a requirement to spend X% of compute on automated alignment research, than other pause or slowdown proposals.
• making the AIs better at alignment research. we might believe that AIs are by default going to be worse at alignment than capabilities, possibly because feedback loops are better for capabilities, or models will be worse at conceptual research, or something like that. if we believe this is fixable, but won't happen by default, then we should make current AIs differentially better at alignment research.
• making yourself better at complementing the skills of AIs. we might think that it will be extremely hard to make AIs differentially better at alignment - maybe AI spikiness is fundamental and requires breakthroughs to change. instead, there will remain some skills (eg research taste) where humans are better than AI, and the supply of human skill here becomes the bottleneck. so you should somehow train yourself to become as good at eg research taste or conceptual research as possible over the next few years, so that when really powerful research AIs come around, you can make much better decisions about which experiments to run. and since almost all relevant research will be done in the future, doing more good research now is much less important than setting yourself up to do more good research later
• do as much conceptual research as possible. we might be so pessimistic about the usefulness of AI for alignment research that we think even once AIs are capable of running experiments way faster, none of that will be useful for alignment whatsoever. maybe you think empirical evidence is just fundamentally not very useful for alignment research and the only real constraint is serial time. then, the only thing that matters is doing as much conceptual research as possible, which means you should start doing conceptual stuff asap and mostly ignore AI assistance until the end, when you invent the One True Metric Of Alignment that you can point the number go up machine at, and AI mostly doesn't help you come up with that metric at all.
• bonus option: aligning current models. you might feel pessimistic about whether the near-future AIs that can automate research will be aligned. maybe you think they will secretly sabotage the research and so the most important thing is to make them not do that. so you should mostly focus on pragmatic alignment of models that we are deploying soon
• bonus bonus option: status quo. maybe you think heavy AI speedup of research is actually far away and the current wave of automated AI research is going to peter out, and then someone will invent some very different paradigm of AI that actually is good at automating research. then you should, idk, work directly on long term alignment research bets the normal way?