First, let me recognize the openness with which you're approaching the problem, and that you've acknowledged there is a problem. My academic background is also applied math, and I believe there is a missing viewpoint that I've been struggling to articulate to colleagues for several years. I'll take your thoughts as an opportunity to try and better understand this view / feeling. If it's alright with you, I'll limit the discussion to applied math, because it's what I know best and where I think the viewpoint is most pertinent.
Full disclosure: your username is very easy to Google, and I should tell you we work on closely related topics. My opinion is shaped in part by several of the papers you've cited. I'm happy to disclose my identity and continue the conversation in private.
You wrote:
"(1) Many academics aren't aware non-academics read their papers at all"
What, then, is the point of applied mathematics? Please know that I don't mean that in a dismissive way. I think there are a few reasonable answers. Chief among them is the belief that exploratory research is important in its own right and does not need to have an immediate non-academic use, as embodied by this quote of Hadamard:
“Practical application is found by not looking for it, and one can say that the whole progress of civilization rests on that principle.”
I believe the above quote as far as it concerns mathematics. But how do we get from there to the applied part? I have an internal dissonance about this that goes deeper than just semantics. Before I started my PhD, I had some vague belief that after writing up some research with an algorithm in it, you'd put it on the arxiv, and from there someone might one day need something like that, code it up, and use it. If I could put in a basic working implementation that was even better.
All the evidence I've seen so far tells me this is not so. The truth is no one is going to take the time to code up your algorithm, because no one has dozens of hours to spend understanding your paper, developing an algorithm suitable for an industrial problem, often just to get improvement on a niche subset of cases. I've been wondering how to estimate the number of algorithms described on the arxiv that are ever implemented and used in a non-academic setting -- my bet is (outside of ML), less than 1%.
I've heard many times that sophisticated higher-order methods for PDEs (finite element / volume, Galerkin, ...) are used in aeronautics, to determine the wind shape over an airplane wing. I've found out from talking to people in the industry at companies like Bombardier that for the most part they do second order finite difference like the rest of us. Why? Because you can code it up in an afternoon, whereas writing the more sophisticated methods can take weeks or months. As academics, we think that the theoretical work is the really hard part, and we neglect the human cost of writing and maintaining algorithms. We have it backwards: academics are (relatively) cheap; code (and changing code) is expensive. (Of course, I make these comments assuming a certain scale. We can come back to this.)
I think the fundamental issue is that I know few applied mathematicians who start with a problem and seek out a solution. Most often, you finish your (applied) math PhD armed with some machinery. If you want to get a professorship and you've done well, you typically turn the crank of your particular machine better and faster than most. In applied math we can say our model is motivated by some problem in the sciences/economics/whatever, but in my experience that just lets us erect a straw person (create a problem) and tear it down (solve the problem) using the machinery that only we have mastered. Just because a problem is hard doesn't make it important.
What to do, then? How do you work on "consequential" problems?
To be pithy about it, I've found it useful to think in terms of $ rather than h-index. In many cases, a consequential problem is one that, if you solve, you can monetize. You could frame this as asking what kind of mathematics could enable new technologies. In my experience it is very difficult to write down a mathematical question that, if answered, can lead to new technology. But if you manage to find such a question -- and it is possible -- it can be a goldmine.
I have more to say -- especially about how mathematicians need to get a reality check on the importance of hardware and its relevance in stochastic algorithms research -- but this is long enough as it is, and I don't want to just be a crazy person rambling in the corner. I'd be very curious to hear your thoughts.