Thanks for making this more concrete! I still disagree with you, but this list provides a good way of articulating why.
Of these, I think the initial case for AI takeover risk was the most impactful by far, and also a great example of introducing a new ontology (which includes concepts like AGI and superintelligence, the orthogonality thesis, instrumental convergence, recursive self-improvement, the nearest unblocked strategy problem, corrigibility, alignment, reward tampering, etc).
The simulation argument, by contrast, is an interesting example of an idea that is nominally very "big if true" but has actually had very little impact. And one reason why I think this is the case is because it doesn't really change our ontologies much. We add the concept of the universe being a simulation, but in order to understand what's inside the simulation we still use all our old concepts, and we have almost no new concepts that help us think about what's outside the simulation. (Off the top of my head, "ancestor simulation" is the only additional novel concept I can recall related to this hypothesis.)
Existential risk and longtermism fall somewhere in the middle. They are also "big if true", and they have been fleshed out to some degree (e.g. with concepts like the vulnerable world hypothesis, astronomical waste, value lock-in, etc). But I don't think it's a coincidence that the vast majority of work under these headings has been on preventing AI takeover. Outside that bucket, I'd say these ontologies are kinda "thin", which has made it difficult to use them to do substantive work without funneling that work through better-developed ontologies (like AI risk).
What do I mean by "thin"? Roughly two things. Firstly, it's unclear if the concepts in them are well-defined or well-grounded. For people on LessWrong, a good way to get a sense of such concepts is from reading continental philosophy, where people often use words in vague ways that feel like they're mostly trying to convey a vibe not a precise meaning. Now, analytic philosophers try to be more precise than continentals. But when reasoning about weird futures, conceptual clarity is extremely difficult to achieve; from a future perspective most strategy/futurism researchers will likely seem as confused as continental philosophers seem to LWers. For example, a concept like "extinction" seems very easy to define. But actually when you start to think about possible edge cases (like: are humans extinct if we've all uploaded? Are we extinct if we've all genetically modified into transhumans? Are we extinct if we're all in cryonics and will wake up later?) it starts to seem possible that maybe "almost all of the action" is in the parts of the concept that we haven't pinned down.
And that becomes much more true when working with far more abstract concepts like "lock-in". If you ask me "will the values that rule the future be locked in?" the majority of my probability mass is on "something will happen which is a very non-central example of either 'yes' or 'no' in your current ontology—in other words, your conception of locked-in is too vague for the question to be meaningful". For more on this, see my post on why I'm not a bayesian. Other concepts which I think are too vague or confused to be very useful for doing strategy research: AGI, LLMs (at what point have we added so much image/video/RL data that summarizing them as "language models" is actively misleading?), "human power grabs" (I expect that there will be strong ambiguity about the extent to which AIs are 'responsible'), "societal epistemics", "alignment", "metaphilosophy", and a range of others.
Secondly, though, even when concepts are well-defined, are they useful? In mathematics you can easily generate concepts which are well-defined on a technical level but totally uninteresting. One intuition pump here is personality tests: it's very easy to score people's personalities on a bunch of different axes, but most of the time those axes are so arbitrary that it's hard to "hook them in" to the rest of our knowledge about how people think. Similarly, even insofar as DeepMind's "levels of AGI" are well-defined, they're just so arbitrary that we shouldn't expect these concepts to carve reality at its joints. But these kinds of frameworks and taxonomies abound in futurism/strategy research.
And so, instead of trying to produce "strategy research", I claim people should try to do the kinds of work that produced powerful ontologies in the past—whether that's inventing theoretical frameworks like probability theory/information theory/computation theory, doing empirical research to produce new scientific fields, doing the kinds of philosophy that produced our current political ontology, etc.