Learning how to create even a simple recommendation engine whose output is constrained by the values of its creators would be a large step forward and would help society today.

I think something showing how to do value learning on a small scale like this would be on topic. It might help to expose the advantages and disadvantages of algorithms like inverse reinforcement learning.

I also agree that, if there are more practical applications of AI safety ideas, this will increase interest and resources devoted to AI safety. I don't really see those applications yet, but I will look out for them. Thanks for bringing this to my attention.

it is demonstrably not the case in history that the fastest way to develop a solution is to ignore all practicalities and work from theory backwards

I don't have a great understanding of the history of engineering, but I get the impression that working from the theory backwards can often be helpful. For example, Turing developed the basics of computer science before sufficiently general computers existed.

My current impression is that solving FAI with a hypercomputer is a fundamentally easier problem that solving it with a bounded computer, and it's hard to say much about the second problem if we haven't made steps towards solving the first one. On the other hand, I do think that concepts developed in the AI field (such as statistical learning theory) can be helpful even for creating unbounded solutions.

AIXI showed that all the complexity of AGI lies in the practicalities, because the pure uncomputable theory is dead simple but utterly divorced from practice.

I would really like it if the pure uncomputable theory of Friendly AI were dead simple!

Anyway, AIXI has been used to develop more practical algorithms. I definitely approach many FAI problems with the mindset that we're going to eventually need to scale this down, and this makes issues like logical uncertainty a lot more difficult. In fact, Paul Christiano has written about tractable logical uncertainty algorithms, which is a form of "scaling down an intractable theory". But it helped to have the theory in the first place before developing this.

an ignore-all-practicalities theory-first approach is useless until it nears completion

Solutions that seem to work for practical systems might fail for superintelligence. For example, perhaps induction can yield acceptable practical solutions for weak AIs, but does not necessarily translate to new contexts that a superintelligence might find itself in (where it has to make pivotal decisions without training data for these types of decisions). But I do think working on these is still useful.

My current trajectory places the first AGI at 10 to 15 years out, and the first self-improving superintelligence shortly thereafter. Will MIRI have practical results in that time frame?

I consider AGI in the next 10-15 years fairly unlikely, but it might be worth having FAI half-solutions by then, just in case. Unfortunately I don't really know a good way to make half-solutions. I would like to hear if you have a plan for making these.

Basically time spent now on unbounded AIXI constructs is probably completely wasted. Real AGIs don't have Solomonoff inductors or anything resembling them.

I wouldn't say that the time studying AIXI-like models is completely wasted, even if real AGIs turned out to have very little to do with AIXI. Even if AIXI approximation isn't the way that actual AGI will be built, to the extent that the behavior of a rational agent resembles the model of AIXI, studying models of AIXI can still give hints of what need to be considered in AGI design. lukeprog and Bill Hibbard advanced this argument in Exploratory Engineering in AI:

...some experts think AIXI approximation isn’t a fruitful path toward human-level AI. Even if that’s true, AIXI is the first model of cross-domain intelligent behavior to be so completely and formally specified that we can use it to make formal arguments about the properties which would obtain in certain classes of hypothetical agents if we could build them today. Moreover, the formality of AIXI-like agents allows researchers to uncover potential safety problems with AI agents of increasingly general capability—problems which could be addressed by additional research, as happened in the field of computer security after Lampson’s article on the confinement problem.

AIXI-like agents model a critical property of future AI systems: that they will need to explore and learn models of the world. This distinguishes AIXI-like agents from current systems that use predefined world models, or learn parameters of predefined world models. Existing verification techniques for autonomous agents (Fisher, Dennis, and Webster 2013) apply only to particular systems, and to avoiding unwanted optima in specific utility functions. In contrast, the problems described below apply to broad classes of agents, such as those that seek to maximize rewards from the environment.

For example, in 2011 Mark Ring and Laurent Orseau analyzed some classes of AIXIlike agents to show that several kinds of advanced agents will maximize their rewards by taking direct control of their input stimuli (Ring and Orseau 2011). To understand what this means, recall the experiments of the 1950s in which rats could push a lever to activate a wire connected to the reward circuitry in their brains. The rats pressed the lever again and again, even to the exclusion of eating. Once the rats were given direct control of the input stimuli to their reward circuitry, they stopped bothering with more indirect ways of stimulating their reward circuitry, such as eating. Some humans also engage in this kind of “wireheading” behavior when they discover that they can directly modify the input stimuli to their brain’s reward circuitry by consuming addictive narcotics. What Ring and Orseau showed was that some classes of artificial agents will wirehead—that is, they will behave like drug addicts.

Fortunately, there may be some ways to avoid the problem. In their 2011 paper, Ring and Orseau showed that some types of agents will resist wireheading. And in 2012, Bill Hibbard (2012) showed that the wireheading problem can also be avoided if three conditions are met: (1) the agent has some foreknowledge of a stochastic environment, (2) the agent uses a utility function instead of a reward function, and (3) we define the agent’s utility function in terms of its internal mental model of the environment. Hibbard’s solution was inspired by thinking about how humans solve the wireheading problem: we can stimulate the reward circuitry in our brains with drugs, yet most of us avoid this temptation because our models of the world tell us that drug addiction will change our motives in ways that are bad according to our current preferences.

Relatedly, Daniel Dewey (2011) showed that in general, AIXI-like agents will locate and modify the parts of their environment that generate their rewards. For example, an agent dependent on rewards from human users will seek to replace those humans with a mechanism that gives rewards more reliably. As a potential solution to this problem, Dewey proposed a new class of agents called value learners, which can be designed to learn and satisfy any initially unknown preferences, so long as the agent’s designers provide it with an idea of what constitutes evidence about those preferences.

I think a very important application of AI safety ideas is self driving cars. This is a domain where traditional AI methods aren't straightforwardly applied. You can't merely have an algorithm take in input and predict what a human would do. Otherwise it will just drive like it predicts a human would. You can't have it get in accidents, so training data is limited.

As people have said at length, AIXI is not a solution even in principle. Hence MIRI's work on an actual theory of AI and FAI. Speaking of, I've said this before, but I'll state it now more starkly: your timeline seems as delusional to me as MIRI apparently seems to you.