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?

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    If you don't know what a Hilbert space is, perhaps you should try and find out. The claim that the mathematics of Hilbert spaces have no practical bearing on power engineering is laughably far from being true. – jwg Aug 25 '17 at 9:23
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    As an electrical engineer, I have seen that in the special case of power engineering, there is nothing much left to do. For example, while the efficiency of most commercial-grade transformers is about 97 percent, I have seen some PhD-level research to increase their efficiency using some wild methods and assumptions. Something that nobody would bother to look at, even the author after publishing. And I have seen that the students in this field are more prone to become philosophically unmotivated. – polfosol Aug 26 '17 at 5:40
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    @polfosol You said it better than I did. This is exactly the sense that I got after reading some of these papers. These papers often use "wild" methods that are not even robust on a theoretical level. I used the example of power because this is where a lot of these methods can go very wrong in practice, anything involving meta-heuristics, genetic and evolutionary algorithms, machine and reinforcement learning. There are extremely legit research directions such as stochastic modeling and convex optimization. I'm not sure what you meant by "philosophically unmotivated" though – Detective Mooch Aug 26 '17 at 9:10
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    At current, a lot of the answers below basically just point out that any sort of research might have non-zero expected value. This observation seems both to be trivial and miss the question's intent by taking "no practical relevance" too literally. – Nat Aug 26 '17 at 13:54
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    @jwg I know what a Hilbert space is, and I don't see where the OP made the “claim that the mathematics of Hilbert spaces have no practical bearing on power engineering”. What I see is 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 — and this seems a fair point (if such a line actually occurred in a paper). – ShreevatsaR Aug 26 '17 at 16:45

14 Answers 14

up vote 174 down vote accepted

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&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.

EU TRLs

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.

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    In my country, grant agencies won't fund anything below TRL3. This is the main reason we have fake applied research. People still do basic research, but they need to dress it as applied. Meanwhile, our industry won't even consider investing into something below TRL9. I think it's not as bad in US, but I'm quite convinced it's one of the reasons OP sees what he's seeing. – Magicsowon Aug 23 '17 at 8:00
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    @DetectiveMooch Are you sure you should build self-learning power grids now? How well do they work in theory? Just from what you say, I'd bet not well enough; if some problems are visible in the theory, those problems can be addressed in the theory first, before the experimentalists get involved. – Blaisorblade Aug 24 '17 at 0:30
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    I'm nitpicking a "glaring example", in your words. I and others have answered elsewhere on unrealistic assumptions. – Blaisorblade Aug 24 '17 at 2:06
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    @DetectiveMooch As I said, bringing things that already exist into practice is largely not the job of academic research. For this, you don't need papers and PhD students - you need a business case, VC funding, and good salesmen. – xLeitix Aug 24 '17 at 6:02
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    @user12956 Aside from a few media luminaries, most researchers don't pretend like they know what the future will be like. By nature, most real research is of the "throw things to the wall and see what sticks" variety. As people here are prone to say: if you already know that it will work, it's not research. I would argue it's the same for impact. – xLeitix Aug 25 '17 at 10:25

Things with "no practical relevance" are not necessarily useless. They may just be "waiting for their time."

For instance, the phenomenon of ionic liquids was first discovered in the early 1900's, but they didn't catch on economically or industrially until the early 2000's when they were "rediscovered" and brought to prominence as "green solvents."

So it's probably unfair to say something has no possible practical relevance. It just might not be obvious yet where they could be used in the future.

Another point to consider is the possibility that someone is engineering but not really doing what is considered "engineering." This may have been a hiring decision, or someone finding a home for where they teach rather than trying to find the right home for their research. (That is the situation for me: I am an engineer by training, but my research could just as easily fit into a chemistry or materials science department.)

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    Good point. It was only after the death of Mendel that people realized the importance of his work. Also, the concept of negative numbers was seen as very absurd for thousands of years. Same with the concept of fractions and decimals. I wonder if Aryabhatta had considered the importance of the invention of the concept of zero. These were all useless concepts at some point of time. But today... – Nav Aug 23 '17 at 16:48
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    I agree that things with "no practical relevance" may be just waiting for their time. I can definitely say this is the case in fields like material science, certainly we have no clue what the possibilities are for the vast majority of newly created meta-materials. However, in engineer fields that are more theoretical, there are often assumptions of infinite amount of times, or limitless amount of information; these things can never come to realization. In some paper you see that, assume "every person in an area has a information receiving device that tells them"...but how can that be? – Detective Mooch Aug 23 '17 at 21:32
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    @DetectiveMooch ever heard of a cellphone? Modern smartphones are exactly "an information recieving device that tells them...", and they're incredibly widespread now in the west – Leliel Aug 23 '17 at 21:54
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    @DetectiveMooch Unrealistic assumptions do not make a result useless — it can't be applied directly, but that's not the goal. Your argument shows that the theory of ideal gases is useless because it's built on unrealistic assumptions. My high school physics suggests that the theory of ideal gases is a stepping stone to more realistic theories. In that case, it's also a decent first approximation of practical gases. – Blaisorblade Aug 23 '17 at 23:50
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    @DetectiveMooch As someone in industry, when I've seen real jumps forward it has been ideas from two dissimilar fields being merged together. So a paper in remote sensing that makes a set of assumptions that are wildly unrealistic for their proposed application might be found by an agronomist who comes up with an idea for using it to efficiently target fertilizer distribution. Even wildly impractical ideas can cross pollinate across domains beautifully. – Myles Aug 25 '17 at 18:07

Research which shows new methods does not have to demonstrate the practicality of the new methods to be useful. An example from something that can be very applied is research in numerical solvers for ODEs. The vast majority of methods which have been created are not used in production-quality ODE solvers. They just aren't efficient. But having a comprehensive literature to pull from can be really helping when trying to learn about the possibilities. Someone outlining a method which isn't very efficient might've contributed new ideas for how to adapt to a certain case that in the future someone else can use to create something that is actually practical. And having a publication which implicitly highlights "look, this thing really only works in special cases because of X" helps someone else in the future when they have that idea (it's much quicker and easier to read a paper and go "okay, that doesn't work as well as I'd hoped" instead of building it yourself).

This also relates back to publication bias. Publishing that something doesn't work is just as valuable as publishing that something does work. Of course, modern publication practices require "significance" so generally researcher have to be sly about how they write the abstract ("we find that in conditions X, Y, Z that this method may be more efficient than current standard choices"), but it's pretty clear from the paper what it actually means in practical terms.

In the end there's a wave of information that moves forward and almost accidentally stumbles upon ideas which work, and these stick and become used in industry. Meanwhile, research continues onward to see what else it can find.

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    Sadly, getting something published about a method that worked not so well is pretty hard. – Geliormth Aug 23 '17 at 9:57
  • Your example of numerical ODE solvers can be extended a bit. Good numerical ODE solvers exploit smoothness of the solution, at least at most points. Stochastic ODEs don't have this smoothness, so adapting the good methods for ODEs to SODEs is pointless--and in fact can create serious issues with things like spurious cross-correlations. The good SODE methods are actually adaptations of the very simple ODE methods. Having these already in the literature at the time that SODE methods were being developed was surely useful. – Ian Aug 23 '17 at 13:51
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    Well, these days most of the good methods for SODEs are not adaptations of simple ODE methods. But the theory for there development draws a lot from ODE theory, and the heuristics like leading truncation error coefficient analysis has been paralleled in SODE literature with great success. These theories were created to answer questions about why some proposed methods ended up not efficient, so those methods have helped many better methods be created via the contrast. You can see the same development in L-B-S stability of implicit RK methods. – Chris Rackauckas Aug 23 '17 at 14:45
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    Another good extension is solving large eigenproblems. Today's "goto" methods are often based on math discovered and published by Arnoldi and Lanczos in the 1950s. In the 1960s this was generally regarded as very interesting theory, but unusable in practice because of the unpredictable accumulation of catastrophic rounding errors. If took another 20 years until cheap and simple methods of zapping those rounding errors were discovered - and probably another 10 years before "non-experts" had access to the algorithms for solving real world practical problems. That's 40 years to reach "level 9!" – alephzero Aug 23 '17 at 21:25

Pseudo-applied science is often a waste of resources. This does not mean that fundamental or basis research is pointless, but there is a difference: Having an abstract model for something "out of reach" can be fruitful - one can study it, and add more obstructions in the future.

But there are seemingly applied models which draw an unnecessarily amount of attention. They are either too simplified and already well-understood so that you should move on to more realistic models or they make totally unrealistic assumptions which allow you to apply a method that would otherwise be infeasible. In both cases the models "survive" in the community because the number of scientists is large enough to form a "peer review group" so that papers get published.

Summarized: Fundamental research is helpful, but beware of constructing "applied models" that do not have applications.

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    Voted up because this is a point worth raising, but I am not sure how "often" is pseudo-applied science a waste of resources. I think that painting research as more applied that it realistically is at the point of writing is hurting science, but it will only stop when we will put less emphasis on applicability when judging research. – Benoît Kloeckner Aug 23 '17 at 13:26
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    More than once I saw a model that was really strange, and after all the argueing why it is "useful", one saw that it was exactly tailored for the solution method that appears later in the paper. If you try to solve the Traveling Salesman Problem as "very abstract version" of transportation, this is fine. If you impose some conditions, argue why they fit "practise" and then reveal that they are needed for specific solution method, you are doing pseudo-applied science. – J. Fabian Meier Aug 23 '17 at 13:37
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    I think this answer really gets to the crux of my question. I am not complaining about engineering research that are published without immediate application, i.e., fundamental research. It is that a significant subset of engineering research purports to solve a host of problems, yet there is very little evidence that it can actually do that beyond what the paper shows. For example, learning algorithms used in mobile communication. It is very difficult to see how humans and their mobile phones conveniently fit into a learning framework, whose behavior can be modelled as learning algorithms. – Detective Mooch Aug 23 '17 at 20:57
  • As an engineer who spends most of my time developing numerical methods (and not publishing the good ones, since I'm in industry and we prefer kicking sand in our competitors' faces to telling the world how smart we are!) "pseudo-applied science" makes me think of economics or psychology more than engineering research ;) – alephzero Aug 23 '17 at 21:32
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    Fabian, I agree with many of your points. However, I think that your answer would be improved if you could define in the answer what you mean by pseudo-applied science. – I Like to Code Aug 24 '17 at 15:39

I think the other answers look at the question in one way, but I'm going to answer it from a more 'human' perspective.

Because it's interesting.

Most people do research because what they're researching interests them. They're not trying to make millions (quite the opposite usually - they're often not well paid); they're not trying to change the world (even if they do so later); they're just really interested in if XYZ is possible.

The fact that sometimes you get something really ground breaking from research that changes how the world works means that companies are willing to invest in the research; but on a personal level, if you're not interested in doing the research, then there's not much point in doing it.

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    Are researchers really not well paid? My sister is currently looking for a postdoc research job in mathematics and apparently most of them offer quite some money. Significantly more than I can get in digital hardware development (generally a well paid field) with my master’s degree. – Michael Aug 25 '17 at 18:52
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    Salaries of researchers vary wildly by field, country, and stage in their career (phd, postdoc, permanent), and also by whether they work for a private or public employer. Some researchers have a great salary, others not so much. However, it is a safe assumptions that a vast majority of researchers do not get into research out of pecuniary interest. – sergut Aug 27 '17 at 13:28
  • Would love to know what part of this the downvoters found not helpful. – UKMonkey Nov 15 '17 at 10:05

A lot of research is currently impractical and theoretical. But that's why lots of it is university research rather than commercial R&D. And sometimes it becomes very useful, eventually.

When semiconductors were discovered back in 1821 no one in their wildest dreams would have realised what an impact they would have.

And Lasers. A great idea to shine a coherent single wavelength light at something: but why would you bother? And they required expensive materials which ruled out every day use. Then semiconductor lasers were discovered. And then fibre optics, which need a coherent single wavelength of light to make a data signal go far. So now all the internet runs over fibre-optic cables fed by tiny cheap lasers, totally revolutionising everything, due to pure research which sounded very unlikely to yield anything useful about 70 years before.

The construction of normal bases of a finite field extension is "far-fetched from practical implementation". It has "very limited practical relevance, and with no attempts to address implementation concerns". Moreover, it is "so mathematical". "It is a legitimate question as to why anyone would ever use these highly-theoretical, and assumption laden research results."

This all is very true. Or, better to say, was very true. In the past.

Until you suddenly had the Massey-Omura cryptosystem.

The fact that it has no application, or proper implementation right now does not mean it will never have one. Who ever used those theoretical things called Riemann manifolds in actual real life? Good thing they were there already by the time Einstein worked on his general relativity.

Theoretical research is there, so that at one day someone else can pick it up and use it.

Why does anybody study drugs on animals? We don't care about healing lab rats. But we hope that helps us study drugs on humans.

Similarly, the goal of solving problems in oversimplified settings (lab rats) is often to help solving those problems in more realistic settings.

Lots of research is not targeted at direct application, but at other researchers. This is a feature, not a bug, because researchers need to build on something. The path from a paper to its application does not need to take a single step. Also, not all of the theoretical papers need be applied. Some of those theoretical results aren't good enough to be applied, and you can tell from the paper itself—more theoretical work is needed before they're worth applying.

Sometimes, even when you know where you want to get, but you have no idea of the path, going in somewhat random directions at the beginning is more effective than targeting the destination directly. (Saw a keynote about a formal study of this in optimization problem).

In a neuroscience class, we discussed how models help understanding the brain. A researcher taught us compellingly that the virtue of a model is not (only) in what it includes, but in what it leaves out. We can't understand a full model of the brain; but we can study oversimplified models to see how they behave, then check if what we learn applies on more realistic models. It also turned out that oversimplified models of the brain are useful as artificial neural networks.

Some of the papers you have seen start from unrealistic assumptions. Likely, that's to simplify their study, especially if it is a mathematical study. Papers in slightly more realistic conditions come afterwards.

While I don't study engineering myself, I study computer science (programming languages), and we also have many papers which consider simplified scenarios—many of those papers are still indirectly relevant, though it can take decades before theory becomes usable in practice.

EDIT: since you ask/question relevance/applicability: I'm thinking of mathematical papers which are motivated (implicitly or explicitly) by the goal of making programs less buggy. Lots of progress relies on doing more math of extremely abstract sorts, but going from math to more math to prototypes takes few stages.

  • I don't understand why you are so defensive. Certainly you have seen papers with very limited or without immediate application, or with very unrealistic assumptions, or have very limited applications. You say that in CS there are many papers that may take decades before theory becomes usable, then why not concentrate effort on making the theory useable? In CS there are definitely more room for non-application driven research, this is not the stated goal of engineering research. – Detective Mooch Aug 24 '17 at 0:37
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    On "Why not concentrate effort", oversimplifying: (1) on some theoretical papers, more theory is what's needed before making the theory usable. My field is full of people applying (arguably) stuff that is completely broken in theory (hence in practice). (2) On other theoretical papers, oversimplifying, the "mathematicians" (think) they're done, and more "practical guys" are welcome to come. At most, the mathematicians can spend more effort to talk to the practical guys, but research isn't a fully coordinated endeavor. – Blaisorblade Aug 24 '17 at 1:59

PhD research is almost by definition part of the education process, rather than part of a product development process, thus the work will appear to have little direct practical relevance.

A similar aspect can happen in industry itself where some of the applied research is directed at the latest buzword aspects, often without a clear understanding as to whether the research will bear fruit (i.e. directly, this year). More usually the work will fall away and become part of the researchers education (just like the 9 out of 10 start-up entrepreneurs).

Knowing if the work will have relevance is hard, but the learning will be useful. I have current work based on 'failed' AR work from 10 years ago..

Remember, feedback control was an invention (H.S.Black) which no-one believed, so some ideas do have their day. Boole was long dead before his (silly) ideas in logic came into fashion.

That all said, it is still wise to be sceptical and think about what will really happen to the ideas, and to what other element is missing from the fanciful studies [Most of the green energy studies will work once an effective industrial battery is developed that can be located near the point of generation, but until then....]

You never know when research with no practical relevance will suddenly become relevant.

A recent example in my field (astrophysics): The BICEP2 results that initially stated they had detected a signal attributable to rapid inflation of the early universe. If this signal proved true, these people would likely have won a Nobel Prize, just to give an idea of how big of a deal this was. However, others recognized that the cosmological "signal" likely could be completely attributed entirely to interstellar dust floating around in the Milky Way. Almost overnight, astrophysicists who specialized in interstellar dust became the world-experts of cosmology. Their research (which I will admit was important and applicable in its own right, so not an exact parallel to the OP's question) all of a sudden became incredibly relevant and important.

Another example is Einstein's theory of General Relativity. Although an incredibly amazing theory in its own right, and extremely useful for understanding the universe, its applications to more "real life"-type situations were for many decades basically non-existent. That is, until GPS was developed. Without accounting for General Relativity effects in GPS measurements and calculations, GPS measurements of positions would quickly become very incorrect. "Errors in global positions would would continue to accumulate at a rate of about 10 kilometers each day!" So decades after a theory was developed, technology finally advanced to a point where the theory became practically relevant in first the military and then our daily lives.

These examples aren't perfect parallels of the situation the OP describes, but still serve to illustrate my original point: you never know when research with no practical relevance will suddenly become relevant.

REASON 1 :

Research is a vast domain where expectation of solution to any particular challenge or inventing a new methodology doesn't come over night. A fully fledged commercial product available is not one scholar's Research Paper published . It's an integrated study , Work of many scholars for decades. The best any knowledged person can do, is to present his contribution on his domain in any medium . With his/her contribution can make a remarkable resource not only in the same domain, sometimes in others too. Sometimes a technical paper can be an inception of new revolutionary technology or ground breaking benefaction for the existing technology. Here the contribution is important than the requirement.

REASON 2 :

Technology is a result of unexpected revolution. There shouldn't be scarcity of resources. Hence abundance of research is going on across the globe in multiple domain as the key for future or present innovation . Everyone's knowledge is precious and valuable. This knowledge cannot be shared through mouth , but only through technical papers for the present and future generations. When any new break through happens , the resources should be ready to serve the purpose.

Research is a lengthy journey and concluding the final result is twice as long and Implementing is thrice as long

How far is it from flying a kite in a thunderstorm to building a lightning rod that can protect a barn? Ben Franklin did both.

How far is it from Claude Shannon's paper on digital encoding of signals to the now familiar audio CD?

It seems to me that basic research has to ask questions, even when it's not clear how the answer will be of benefit. Sometimes, the research turns out to be science research instead of engineering research, as in the kite example above. But you get the idea.

Perhaps applied research is more down your alley than basic research.

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    Ben Franklin and Claude Shannon are bad examples as their work was widely recognized as highly valuable in their own time. – Nat Aug 26 '17 at 14:01

"Usefulness" is about perspective and perception. In my own little office cubicle maybe it is difficult to see where exactly my research results fit in. Just try and find confidence in that there exist (more or less visible) visionaries "high up" in different aspects who see where it will fit in. The bad thing about religion being so bashed and marginalized these days is that the concept of faith in things larger than us loses significance while in practice it is more relevant than ever. Maybe not in an almighty God, but in the existence of people making plans outside of ones' own perspective.

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    While I can appreciate faith having some relevance beyond just religious impact, this particular answer seems phrased in a way that gives undue credit to ruling out the good of the religious impact. – TOOGAM Aug 25 '17 at 5:00

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