Thanks for continuing to engage.
I described my position in another comment. To reiterate and elaborate:
My current best guess is that there are so many unrelated potential models for AI (relative to the information that we currently have) that the probability of FAI work on a single one of them ending up being relevant is tiny. In order to make a compelling argument for the relevance of MIRI's work on the Lob problem, you have to argue that the model used isn't only one of, e.g. 10^10 distinct models of AI with similar probability of being realized in practice.
One could argue that the problem is sufficiently important so that one should work on it even if the probability of the work being relevant is tiny. But there are other interventions on the table. You've made major contributions by spreading rationality and by creating a community for people who are interested in global welfare to network and collaborate with one another. These things probably substantially reduce astronomical waste (in expectation). In order to argue in favor of MIRI's FAI research being optimal philanthropy, you have to argue that the probability of the research being relevant is sufficiently great so that its expected value outweighs the expected value of these other activities.
One could argue that if there are in fact so many models for AI then we're doomed anyway, so we should assume that there aren't so many models. But rather than trying to work on the models that we think most relevant now, we can wait until it becomes more clear what AGI will look like in practice, and then develop FAI for that type of AI. Whether or not this is feasible is of course related to the question of whether the world's elites will navigate the creation of AI just fine. I think that there are good reasons to think that the probability of this is pretty high, and that the most leveraged efforts are getting good people in positions of future influence rather than doing FAI research now. Your work on rationality training and community building can help, and already has helped a lot with this.
Neither 2 nor 3 is the sort of argument I would ever make (there's such a thing as an attempted steelman which by virtue of its obvious weakness doesn't really help). You already know(?) that I vehemently reject all attempts to multiply tiny probabilities by large utilities in real-life practice, or to claim that the most probable assumption about a background epistemic question leads to a forgone doom and use this to justify its improbable negation. The part at which you lost me is of course part 1.
I still don't understand what you could be thinking her...
An early draft of publication #2 in the Open Problems in Friendly AI series is now available: Tiling Agents for Self-Modifying AI, and the Lobian Obstacle. ~20,000 words, aimed at mathematicians or the highly mathematically literate. The research reported on was conducted by Yudkowsky and Herreshoff, substantially refined at the November 2012 MIRI Workshop with Mihaly Barasz and Paul Christiano, and refined further at the April 2013 MIRI Workshop.
Abstract:
We model self-modi cation in AI by introducing 'tiling' agents whose decision systems will approve the construction of highly similar agents, creating a repeating pattern (including similarity of the off spring's goals). Constructing a formalism in the most straightforward way produces a Godelian difficulty, the Lobian obstacle. By technical methods we demonstrate the possibility of avoiding this obstacle, but the underlying puzzles of rational coherence are thus only partially addressed. We extend the formalism to partially unknown deterministic environments, and show a very crude extension to probabilistic environments and expected utility; but the problem of finding a fundamental decision criterion for self-modifying probabilistic agents remains open.
Commenting here is the preferred venue for discussion of the paper. This is an early draft and has not been reviewed, so it may contain mathematical errors, and reporting of these will be much appreciated.
The overall agenda of the paper is introduce the conceptual notion of a self-reproducing decision pattern which includes reproduction of the goal or utility function, by exposing a particular possible problem with a tiling logical decision pattern and coming up with some partial technical solutions. This then makes it conceptually much clearer to point out the even deeper problems with "We can't yet describe a probabilistic way to do this because of non-monotonicity" and "We don't have a good bounded way to do this because maximization is impossible, satisficing is too weak and Schmidhuber's swapping criterion is underspecified." The paper uses first-order logic (FOL) because FOL has a lot of useful standard machinery for reflection which we can then invoke; in real life, FOL is of course a poor representational fit to most real-world environments outside a human-constructed computer chip with thermodynamically expensive crisp variable states.
As further background, the idea that something-like-proof might be relevant to Friendly AI is not about achieving some chimera of absolute safety-feeling, but rather about the idea that the total probability of catastrophic failure should not have a significant conditionally independent component on each self-modification, and that self-modification will (at least in initial stages) take place within the highly deterministic environment of a computer chip. This means that statistical testing methods (e.g. an evolutionary algorithm's evaluation of average fitness on a set of test problems) are not suitable for self-modifications which can potentially induce catastrophic failure (e.g. of parts of code that can affect the representation or interpretation of the goals). Mathematical proofs have the property that they are as strong as their axioms and have no significant conditionally independent per-step failure probability if their axioms are semantically true, which suggests that something like mathematical reasoning may be appropriate for certain particular types of self-modification during some developmental stages.
Thus the content of the paper is very far off from how a realistic AI would work, but conversely, if you can't even answer the kinds of simple problems posed within the paper (both those we partially solve and those we only pose) then you must be very far off from being able to build a stable self-modifying AI. Being able to say how to build a theoretical device that would play perfect chess given infinite computing power, is very far off from the ability to build Deep Blue. However, if you can't even say how to play perfect chess given infinite computing power, you are confused about the rules of the chess or the structure of chess-playing computation in a way that would make it entirely hopeless for you to figure out how to build a bounded chess-player. Thus "In real life we're always bounded" is no excuse for not being able to solve the much simpler unbounded form of the problem, and being able to describe the infinite chess-player would be substantial and useful conceptual progress compared to not being able to do that. We can't be absolutely certain that an analogous situation holds between solving the challenges posed in the paper, and realistic self-modifying AIs with stable goal systems, but every line of investigation has to start somewhere.
Parts of the paper will be easier to understand if you've read Highly Advanced Epistemology 101 For Beginners including the parts on correspondence theories of truth (relevant to section 6) and model-theoretic semantics of logic (relevant to 3, 4, and 6), and there are footnotes intended to make the paper somewhat more accessible than usual, but the paper is still essentially aimed at mathematically sophisticated readers.