Yes, when as a math grad student I saw some of that, I developed some opinions and ideas to look for more productive approaches.

Somewhere I read: "There is a famous recipe for rabbit stew that starts out, 'First catch a rabbit'.", and I changed that to, "There is a recipe for how to do applied mathematics, first get an application.".

For more, commonly the main criteria for 'research' is that it be "new, correct, and significant". And quite broadly in some powerful places, e.g., a famous David report, there were complaints that a result in math that met the first two but had no visible applications, inside or outside math, was likely short on "significant". So, eventually it dawned on me that if start with an application (something significant in the real world, although inside math would do also but tends to be more difficult and less highly valued outside math) and get a good solution for that application, then have "significant" handled. Yes, these thoughts did occur to me, but they were only secondary: My real interest was 'significant' outside of math and, in particular, in my bank account.

So, on to "new, correct": In math, "correct" is comparatively easy -- just work in the style of definitions, theorems, and proofs where it is fairly easy to check math correctness.

That leaves the part "new": Surprise! If start with a significant problem from the real world, then likely there is no solid solution for that problem on the shelves of the research libraries. Why? Because it's a really complicated real world out there! So, find in your real problem where current math doesn't really provide a solution and then do some more math to get some math for a better solution for the real problem. Now maybe the math just did that was "new" is not as earth shaking for pure math as, say, resolving the Riemann hypothesis, or, now, P versus NP, but still have covered "new, correct, and significant" and, besides, may have something powerful and valuable for the real problem outside math.

And that new math result got for that one real problem has a nice property: Given a new result in 'pure' math, the probability of an application in the next 12 months is small. Given a new result in math that has an application, the probability of another application in the next 12 months is nicely higher. Moreover, that probability appears to be monotone increasing with the number of known applications. Indeed, one skeptical way to evaluate such a result is to look for two significant applications instead of just one!

There is more going for this approach: Are taking math directions and 'values' based heavily on what solves some problems outside math. Well, where'd we get calculus? Sure, trying to make sense out of elliptical orbits of planets. And calculus is the main well spring of the part of math called 'analysis' that is so far by a wide margin the most applicable part of math (I know, number theory can do good things for computer security; maybe some people studying string theory in physics will want some topology; and people in logic may value work in foundations). But, tough not to notice that calculus led to the study of heat flow and Fourier theory which did great things for signal processing.

But in part the OP is correct: When I went through measure theory, it seemed fantastic stuff, especially since finally I had a better theory of integration for applications. But in Rudin's 'Real and Complex Analysis' he discussed regular Borel measures, and I never saw just why he cared about the 'regular'. Maybe if I'd go back and think about those few pages for a few days I'd see it. Yet, if I did see it, then I'd write it down so I wouldn't have to work to see it again, and I wish that Rudin had done that in his book. The precise definitions, theorems, and proofs are crucial, but too often pure math is written with too little explanation of the view from 50,000 feet.

My view is that the key to much more value from computing over the next few decades will be some novel uses of math and its techniques of definitions, theorems, and proofs. Why? Because for what to do in building our hardware and system software, applications, and larger systems, we need more powerful tools than intuitive heuristics or just programming what in principle we see how to do manually.

So, right, in the short term, my approach to math is to do 'applied' math where essentially we start with an application. Then in the longer term my hope is that such math, as calculus did, will lead to new, grand, powerful structures in pure math.

Yes, if the pure mathematicians can make good progress as isolated from applications as in the OP, then good for them, but I concluded that, in effect, good math needs some good applications from outside math.

Much of this 'philosophy' has come to pass whether deliberately or not: Quite broadly it is accepted that the best research 'mathematizes' its field. So, yes, the leading example is mathematical physics, but math is now just crucial in mechanical, electrical, electronic, and civil engineering, statistics, and operations research. Other fields that try to be more mathematical include finance, economics, psychology, sociology, and, now, genetics. And of course computer science is becoming increasingly mathematical.

As powerful as math has been for these other fields, pure math has essentially been left suffering as the applications, grants, and students based on applications of math go to fields outside math. So, if I were a chair or a dean over a math department, then I would welcome serious attention on important problems from outside math. I would keep fully high standards of definitions, theorems, and proofs. But, for more, first cut it would seem that the criteria "new, correct, and significant" would be easier than those criteria with also "applicable, powerful, and valuable" outside of math, but my view is that this is false, that being applicable is easier just to publishable papers but more importantly to real significance both inside and outside math.