Concerns about the value of the research domain

Question

I am a PhD student in applied computer science methods, halfway through the program, and the question that is in the title is what have occupied my mind almost from the beginning of my study. I can't find much help from my supervisors, and this is putting the whole pursuit of my degree under question.

I have read some literature in the domain of my research, and most of the time my critical thinking is not satisfied with what the authors have achieved in the end of their work. Somehow, the conclusions do not seem convincing to me. In my understanding, the idea of a scientific article is to be useful, but what I see in my field of applicational studies is that the articles suggest no real applications, rather some dull scientific examples, saying that it demonstrates its usefullness. Applicational studies should have real applications, not examples in a vacuum.

And it is the same thing, if not worse, in almost all the articles. It gets worse if they start to overcomplicate things, adding one method on top of another to achieve no evident benefit at the end. For me, such research seems like they cannot find a good problem.

Is it just an impression of a sceptic, or could it be that my subfield of research has reached the point where it has closed on itself? I mean, producing papers not to investigate real problems, but just to keep the field afloat, although it has no potential for anything innovative.

I am just starting to doubt that research itself has some special value, as it seemed to me in my idealistic view when I just started my PhD. At this point, I am overwhelmed with the thought that the years that I am spending on my PhD eventually will result with a similar contribution: It will have no use or value. Maybe except to support my supervisor's career and add to the mess of the literature of my domain, where I already have sunk.

So my question for you is: What does motivate you or give you certitude that the things that you work on do have impact, and the work is worth working on?

Answer 1

I cannot possibly agree with the currently most upvoted answer by Pete L. Clark. I clearly cannot comment on the particular subfield that OP is asking about since I know nothing about it.

However, daily I see stillborn research papers --- they were conceived not to dispel the ignorance, but to be added to a CV. There are definitely research communities that are mired in posturing, complexity and obscurantism.

On a personal level, it does not matter whether the field in question is one such area, or whether the OP lacks the background to see how this field adds to our knowledge. It is impossible to do good research without seeing the goal. So, action is necessary.

I suggest talking to the advisor, and gently asking these questions. If the answers are not enlightening, change field/advisor. Doing otherwise is a waste of OP's time.

Answer 2

In my understanding the idea of a scientific article is to be useful[.]

That is not my understanding of a scientific article (or, more basically, of science). Science is a growing body of knowledge and understanding achieved by a characteristic method, and a scientific article adds to this knowledge and understanding. (Roughly; scientific articles can also critique or falsify...) Who said it had to be useful? It is always more useful to have scientific knowledge than not to have it, and many branches of science are easily applied, but by no means all: e.g. up until relatively recently it was believed but not observed that there were exoplanets, i.e., planets outside our own solar system. The first confirmed detection of an exoplanet was in 1992. This was surely one of the major events in the history of astronomy, but...what is it useful for? Something big a thousand years from now maybe, but nothing now.

I have read some literature in the domain of my research, and almost always my critical thinking is not satisfied with what the authors have achieved in the end of their work. Somehow the conclusions seems for me not convincing.

To be honest, I am skeptical of this. Academic fields are built by intelligent, serious, hard-working people, often over the course of several lifetimes. What counts as methodological rigor in one academic field may not in another, but that's not the same thing. If as a mid-career grad student you find that most of the papers you are reading are pointless and limited in a way that you think you see through...anything is possible, but I am going to guess that you are missing something.

Is it just an impression of a sceptic or it could be that my subfield of research has reached the point where it has closed on itself (producing papers not to investingate real problems but just to keep the field afloat alrhough it has no potential for anything innovative)?

I have not in my lifetime met a scientific (or other academic) field where the grad students can tell that nothing deep is going on. It is true that different fields at different times progress in different ways: periods of fundamental advances alternate with periods of more modest improvements and aggregation of knowledge. But they all survive.

To me it sounds like you are just not intellectually interested in your academic field (or the sub-sub-... part of it you're currently occupied). You write:

I am just starting to doubt that research itself has some special value, as it seemed to me in my idealistic view when I just started my PhD. At this point I am overwhelmed with the thought that the years that I am spending on my PhD eventually will result with a similar contribution, there will be no use or value of which. May be except to support my supervisor's career and add to the mess of the literature of my domain where I already have sunk.

In my experience, younger students tend to idealize and elevate academic research as though it were something sacred. When I was a young student of mathematics, I explained why I liked mathematics in terms of its objectivity, its timelessness, and so forth. I don't say much of that anymore -- and not really because I don't believe it: I still do. But I don't believe that it explains why I did mathematics, because the explanation is not enough. There is a lot of mathematics out there; I try to appreciate all of it, but I don't do all of it. Obviously I did not become a number theorist rather than a differential geometer because number theory is more objective or timeless -- or useful! -- than differential geometry. I became a number theorist because I like (and understand, and have a proclivity for) number theory more than differential geometry. There's an ineffability there that we may as well be honest about.

I hope you see the point of that personal digression: I suspect that you simply are not interested in your subfield of applied CS and are therefore searching for more sweeping intellectual explanations of that. But you don't need to -- if you don't like it, you don't like it, and that has to be respected, in particular by you. No, you should not continue in a field just to bolster your supervisor's research career. So it's probably time for a change: whether a small change or a big change I leave up to you, but an intellectual defense of the value of Academic Field X is almost certainly not the answer.

Good luck.

Answer 3

"That's why it's always worth having a few philosophers around the place. One minute it's all is Truth Beauty and is Beauty Truth, and Does a Falling Tree in the Forest Make a Sound if There's No one There to Hear It, and then just when you think they're going to start dribbling one of 'em says, Incidentally, putting a thirty-foot parabolic reflector on a high place to shoot the rays of the sun at an enemy's ships would be a very interesting demonstration of optical principles..." -- Terry Pratchett, Small Gods (Discworld) (1992)

"The release of atomic power has changed everything except our way of thinking ... the solution to this problem lies in the heart of mankind. If only I had known, I should have become a watchmaker." -- Albert Einstein (1945)

"No one has yet discovered any warlike purpose to be served by the theory of numbers or relativity, and it seems unlikely that anyone will do so for many years." -- G.H. Hardy, A Mathematician's Apology (1941)

This is the fundamental conundrum of doing research. You hope that the research you are doing will revolutionize the world, and write grant proposals to that effect, but it's really a crapshoot. Maybe you'll hit a breakthrough; maybe your contributions will languish forgotten on shelves. Maybe someday your works will be dusted off when it is realized that they are exactly what is needed to advance humanity. You just don't know; "practical" applications are usually years off at best.

So what are you supposed to do in the meantime? In my experience, it has to be a question of extrinsic versus intrinsic motivation. Presumably you were excited about your field when you started your PhD. You decided to devote years of your life to the study of a single subject...why? Mathematicians worked on number theory for hundreds of years before RSA and SHA; Einstein never saw photovoltaic solar panels in wide use; Alan Turing never wrote a single program in C++, Java, Haskell, or Python. What kept them going?

Answer 4

It will have no use or value. Maybe except to support my supervisor's career...

I have seen that happen many times. It won't be too terrible if it happens again in your case. Not many people get lucky to hit the bull's eye in their PhD program. Most learn how to do research researching something that turns out to be irrelevant. They publish a paper or two that few people will ever read and get their degree. The real result is the research skills that you will use a lot and improve throughout your career. I would just go with it and try to make the best out of it.

Answer 5

@Pete L. Clark gives you a great answer that, I believe, helps you to see where you are and where you may want go.

In case you're still holding ground on what you think about your field, then I suggest you to see that as an opportunity to do better than the others around, to bring new things to your field. Try to answer this: what can I do to advance the research in my field? If you are certain that the current research is poor, then you are seeing its flaws and you have a good chance to give great contribution.

Answer 6

Having worked in an applied algorithmic field as well, I fully understand the problems of the OP. My experiences:

• Many "applied" papers are not applied in the sense that they consider problems that are asked in the "real world". They may be modelled on real world problems, but in such an abstract way that you cannot use the results to e.g. implement them into some practical useful software. "Applied" is a very wide range.

• Most research areas are driven by peer review. If a group of people like an approach, this approach will survive and more papers are produced in this direction. This includes the danger of overestimating the value of a certain method or drawing questionable answers from inconclusive data. Nonreproducible results on many experimental fields often result from overconfident use of statistics.

• Many grad students work pretty much on their own and therefore have difficulties to distinguish good from bad papers -- the bad ones are just too many.

Nevertheless, there is progress in nearly every field of science, but -- in my opinion -- it can be buried in a large amount of fairly disappointing papers.

Answer 7

I will add a somewhat optimistic answer.

There are a lot of "bad" papers written, in every field; those which are poorly constructed, those with errors, those struggling to find a reason to exist, those published to pad someone's CV, those published for political reasons, etc.

However, think of research as a creative pursuit. Do you think that music or art is not worth it, even though most of it is "bad"? Most of it is trying something that won't work, or it's copying someone else, or it's boring, or it's unclear. Once in a while, something truly special comes along, though; to some people, that's worth it.

As a researcher, you need to learn to separate the good ideas from the bad - there are good papers out there, I promise you. It's likely that many of these bad papers you're reading cite them; follow the citations back. Find the gems and study those hard.

Finally, you can tell that most of what you're reading is bad, which implies that you can tell what is good. Take advantage of that skill!

Answer 8

When I was studying math, discussion was made of pure and applied mathematics. To top-notch pure mathematics culture, it is almost a matter of pride to create research not used in applied math, and a loss of honor, so to speak, if an applied mathematician finds a practical use for your research.

One point which was underscored repeatedly was that not only is applied math finding uses for the most esoteric math you can find, but the time lag between pure math discovery and applied math application was shrinking, and something like 2-3 decades as of the years of my program.

People have come up with examples of mathematical research that is so obscure it will never be applied; one such prominent example is group theory, and I remember it being all the more striking when a friend studying chemistry referred to "the group of rotations of a molecule." She was using the term correctly, it was properly an application of group theory, and it was concrete enough to be used in this way by (nonmathematician) scientists.

Make your computer science work as obscure as you like, but it will probably end up seeing practical use.

Answer 9

This is a common view on first getting really stuck in to the literature, when you realise just how small the increments by which we actually work can be.

You've started to see your own work in the same light. That's normal too. But very few theses are actually a significant contribution to human knowledge. By the end of your PhD, the world will have one more computer scientist -- you -- who will be able to work on a wide range of problems, even if a small part of any of them.

Note that unlike some answers I make the perhaps unrealistic assumption of good faith. The only effect of the pressure to publish frequently is to exaggerate the incremental nature of progress -- but then the results are out there sooner for others to build on.

Answer 10

If your applied field isn't applicable to the real world, the least it could do is change its name. It's also possible that that path of research is a dead end - it wouldn't be the first time in human history that people went the wrong way intellectually.

What would a research domain gone wrong look like? Probably as you describe - the next generation loses faith and questions whether to abandon it. It's possible you're correct and you're at the forefront of this point, another possibility is you could be wrong and just don't get the field. I don't know.

Be true to yourself and be aware of both the sunk cost fallacy and the fact that you have sunk some costs. Depending on how much time you've spent, and whether you can switch to a different topic, you may want to finish and grab the credentials. You'll be a much more formidable critic of the field once you achieve that, but of course by then maybe you'll believe it, whether it's true or not :)