What good is engineering research with no practical relevance? I am a Ph.D. student currently doing research at a top engineering school in North America.

I am becoming more and more jaded at the fact that a sizable portion of the research conducted at my university as well as publications to engineering conferences seem to have very limited practical relevance, and with no attempts to address implementation concerns. Many of these papers seem to be published just for the sake of it. 


One glaring example is power engineering. The methodologies
proposed by recent graduates from power engineering are so extremely far-fetched from practical implementation, it raises the question as to why any such
research should be continued.

Power is a very safety critical field: people can die after going for too long without power (case in point), and the industry itself is highly government regulated. The algorithms that have been proposed from my
research department as well as many like it completely ignore things
like safety guarantees. Furthermore, it is highly unlikely that
government employees in the power industry would rely on some biology
motivated or learning based algorithm to arrange the power supply to millions of actual
people. There are decades old well-regulated power markets for that!
But power is just one example out of many. I have read many papers on
signal processing and control theory. Most of the papers are completely
math and proof based; their proposed methods are so mathematical, with extremely limited robustness or safety guarantees, etc. These researchers are more concerned with epsilons and deltas than how their proposed methods can be realistically
implemented in people's cars or mobile phones. 

An "implementation"
nowadays is just a MATLAB simulation, a few equations, and a graph. Even during undergraduate
engineering training, we have seen how difficult it is to go from
simulation to actual software/hardware that people can use. I can easily show you highly technical papers from these fields published by people who do not even care about the readability of their notation, let alone practical implementation. 
So it is a legitimate question as to why anyone would ever use these
highly-theoretical, and assumption laden research results. It is
unclear what "the small-gain signal must belong to a Hilbert space on
the extended half-line" actually means in real life cache design. Furthermore, many
papers are completely without any mention of practical implementation of
the algorithms, so it is completely unknown if anyone would actually
be able to use these research results. 




Engineering research is ultimately used to create new technologies that promise to improve the lives of people. However, it is unknown to me at this point how a "bat-echolocation based meta-heuristic algorithm for nuclear generator dispatch" could benefit anyone. 

So my question boils down to how we as researchers should attempt to bridge the gap between the highly mathematical, highly theoretical modern engineering research and the practical implementation of research results. What good is engineering research with no practical relevance?
The short answer to your question is that you are vastly overestimating your, and other engineer's, ability to judge what techniques will ever have practical relevance.

I think it was Michael Stonebraker, a Turing award winning computer scientist with no lack of practical impact, who said that the sweet spot for academic applied research are techniques that are about 10 years away from being widely implementable. If you limit yourself to things that you can already do today, you will fail to propose the kind of radically new developments that should, at least in theory, distinguish academic research from other drivers of innovation, such as startup companies or industrial R&amp;D. Incidentally, if the lack of impact your work has right now is distressing you, you should ponder the question whether you would not achieve higher job satisfaction in a startup or industrial lab.

I find your example of self-learning power grids particularly unconvincing. If we rewind time a few years and relate your arguments to research into automated driving, I am sure you will find plenty of people who found this research to be a waste of time. Driving surely is a safety critical field, and automotive is highly regulated. Algorithms for automated driving assistance completely failed to, and to some extent still fail to, address the practical concerns of many stakeholders as well as governmental safety guarantees. And yet here we are. I am not sure if the same will happen to power grids, but it is absolutely plausible that it will.

You may also be interested in reading into TRLs (technology readiness levels), as used for instance by the European Union's framework programmes as well as NASA.



The basic concept here is that academic research is usually best suited to bring ideas from TRL 0 or 1 to 3 or 4. The "Matlab implementations" you complain about may very well just be the laboratory tests that are meant on TRL 3. This is very much in line with the position in the grander scheme of the progress of technology that many large organizations envision for academic research labs.