I recently came across a problem related to image recognition in Deep Learning. One fine morning, I was struck with the idea that possibly I could do something about it if I merged GANs with CNNs. As of now, I only know what these networks are capable of.

Now how should I go about this? Should I first pick a standard book (say Ian Goodfellow's Deep Learning) and read it from cover to cover? Or should I straightaway read some research articles, identify areas I am weak in, and then dig deep into those very areas from standard texts.

In other words, is it better to complete everything I can get my hands on before starting to work on this idea? Or should I start on it and fill the gaps as they come by.

P.S. My background in courses in statistical learning, probability, and calculus ensures I can completely understand the math behind the above stated topics.

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    A discussion to have with your advisor?
    – Solar Mike
    Apr 1, 2019 at 8:24
  • @Solar Mike: Thank you for your comment. I would definitely have discussed, but I don't have an advisor in my college or someone who directs undergraduates in Deep Learning; they aren't specialised in it. So unfortunately, they tell me they would not be able to help me out in this case. Apr 1, 2019 at 9:03
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    I generally start by looking for and reading review articles in the field. If, when I try to read the review articles, I find that I don't have enough background in the basics to understand the review papers then I will look for a broader overview such as a book. Even then, I will usually try to read selected chapters closely relevant to the topic of interest before resorting to reading a book cover to cover.
    – Matt
    Apr 1, 2019 at 13:53
  • @Matt Thanks for your comment. After all the answers and your comment, I too feel now it will be more productive to follow the approach you have suggested. Thanks! Apr 2, 2019 at 1:20

3 Answers 3


I am still learning, but this is how a few advisors taught me how to approach my field.

First, look for a recent structured literature review of the filed and taxonomies. They give you a good starting point as all relevant paper (hopefully anyway) are listed there, and this gives you a perfect index to learn about the filed. Of cause, if there is none, you could be the first to create one ;).

Then its time to read a lot, create a stack of all relevant paper — Mark of any references that look to help and add them to the stack. Keep going and once your stack starts to shrink more than it grows you should have a grasp about the filed.

In order to do this in a reasonable time you do not have to read every paper deeply. Try to get the idea, and try to fit them into your understanding of the filed. Only read paper deeply that help you further your research question, other just skim.

Other tested methods include: Ask your advisor and other colleagues in around you, they might have looked into it already and can point you to relevant material.

  • Thanks for your answer. This stack technique feels cool to me. I'll give it a try in my next literature search process. Apr 2, 2019 at 1:01

You are actually asking the question that most new grad students ask: how do I find, understand, and make an impact on a relevant problem in my chosen field of study? Most grad students are new to "the" field in some way. For instance, you say you have a background in stats etc, so you aren't totally new to the field, you are just new to the specific sub-problem. This gives you a big advantage over someone coming in from a totally unrelated field, like zoology :-P

tawalaya's answer is great and is the basics of how to conduct a solid literature review. The basic underlying idea is you focus on learning as much as possible so that you are no longer new to the field. I'd like to add on to it with a few caveats:

  1. In your literature review, pay special attention to whether or not your solution counts as a contribution to the field or an application of it. This will in large part depend on which field you choose to make an impact in. Is the field deep learning? Image recognition? CNNs? What is a contribution in one field might be just a basic application in another. For instance, if you are trying to make an impact in deep learning but your contribution is just "I put these two nets together and look at how good they solve a specific problem", it's unlikely you'll make an impact. However, if your chosen field is image recognition and you prove theoretically that your network has properties that solve a known problem, it might be a big impact.

  2. Watch out for people who have thought of this before. The unfortunate problem of academic research is that if you thought of it probably someone else has, too. Look far and wide to see if your specific solution, or something so similar to it to make no difference, has already been published or studied and cast aside. It's possible that the idea you think will work is actually no better than another, simpler idea. It's also possible that someone did a similar piece of work to your own and their paper just wasn't impactful enough to draw attention. This might happen because it's not interesting enough or because they published in a low-tier journal.

  3. Be careful about merging techniques. In much of academic research, simply putting two things together and seeing what happens is not sufficient. You should look for how to prove that these two specific things, when put together, are demonstrably better. In your example, why, specifically, should GANs and CNNs be merged to solve this problem? Why not two other things? Why not additional things? How will you know that your network is better?

Ultimately, you're going to have to do more than just learn the field. You'll need to learn to distinguish and sell the value of your research to experienced researchers in the field.

  • Thanks for your answer. It was really helpful. I'll keep these points in mind. Apr 2, 2019 at 1:05
  • Can you please explain what you meant when you said merging the nets to make a contribution in Deep Learning is unlikely to make an impact, while the same theoretical proof that such a merger solves a problem might be a big impact in Image recognition. Are you trying to discuss about the idea of narrowing the focus of study in a research problem- the more focussed the research problem is, the better it is. Apr 2, 2019 at 1:11
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    Basically what I mean is that it's not a contribution to just put two things together and see what happens. That's just an application. Doing research in many fields might involve putting two new things together, but in order to get published you'll need to explain why, specifically and theoretically, this was a good idea. You usually need to prove that these two things, and not some other two arbitrary things, will for sure improve performance and that no one has ever thought of it before. Otherwise it's just playing with software Apr 2, 2019 at 14:02

Other early answers here have focused more on how to learn the field. This will be a bit different. There is, in my opinion, no reason to wait before trying out your research ideas. You will probably never stop waiting if you take that too far. But working blind is likely to lead to dead ends and you need to recognize (or get advice) when you are going down a blind alley.

So, it might be a better path to take a blended approach. Start out by spending some of your time (say 10 - 20%) working on your problem and the rest learning the field and reflecting back on the problem based on what you learn. Over time increase the research portion as you gain experience and spend less on reading the literature.

I doubt that such "research attempts" will be wasted even if they are unsuccessful. You will learn a lot about what doesn't work, at least.

I think that too many students wait too long to start working on meaningful problems. Of course, it is helpful to have an advisor to guide you initially on what is meaningful and what approaches might be tried (or have already be exhausted). If you have ideas, you should spend a bit of time on them, but be critical in your self analysis of what you have, not jumping to conclusions.

But you probably also would benefit from advice. If you don't have a formal advisor then you may still be able to bounce ideas off of a faculty member or other researcher in the field. Practice with feedback is a great way to learn.

  • I think that too many students wait too long to start working on meaningful problems This was my major concern that led me to write this post. Thanks for your answer. I'll look for possible feedback sources. Apr 2, 2019 at 1:00

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