Discovered Phd topic has already been worked on

Question

I am a second-year French Ph.D. student and two days ago I found out the topic I had been working on has already been studied, and the result I wanted to prove is basically already known. Unfortunately, neither I nor the supervisor were aware of this, and when looking at the literature I didn't find this out because it is formulated in a slightly different language than our own, and that's why we didn't find anything for so long. My bad, I should have looked more thoroughly, we only found this out by accident, I should have been more careful since this article is cited in other articles I was referring to. Anyway, what has already been done isn't EXACTLY what I want to do, the setting is different, but the conclusion is practically the same, apart from the different setting (even worse, I think my hypotheses need to be a little more restrictive).

Now, this is bad, I know it. But according to my supervisor, a different approach to look at a problem can be in itself interesting, although it is very much less interesting than it would have been if there hadn't been the other proof. Even more so since (apparently) my approach is worse! My question is: have you ever been in a similar position? What are your sincere thoughts on this? I feel like this is completely meaningless, and that there's little hope to one day find post-doc positions since my work is, to sum up, not new but rather a rediscovery of something but in another (less convenient, apparently) formulation. At the same time, the idea of throwing everything in the bin and starting all over is very, very scary and demoralising.

Answer 1

Something very similar, but much less dire, had happened to me. Perhaps my story below will be of some use, maybe even encouragement, for you.

In July 2011 (nearly 12 years ago, yikes) my advisor assigned me the problem that would ultimately form the basis of my thesis, which was to extend a result due to D.R. Heath-Brown (https://arxiv.org/abs/1103.2028, now published by Q.J. Math: Power-free values of polynomials) to the case of binary forms. Unfortunately, a mere 4 months later, I discovered that Tim Browning had already published such an improvement (Power-free values of polynomials; same title, but different paper/author).

I was quite discouraged, but my advisor Cam Stewart essentially told me that the bar has simply been lifted higher, but the reward will now be greater. Ultimately I ended up improving on Browning's result (Power-free values of binary forms and the global determinant method). This ended up impressing Heath-Brown, who then agreed to take me on as a postdoc after graduation.

Answer 2

Every mathematician has had the experience of being "scooped," and it's never a pleasant feeling. As you can see from the many upvotes, we all sympathize with your situation.

Objectively, though, the situation is probably nowhere near as bad as it might seem to you right now. As Zach Teitler mentioned in a comment, the fact that someone else has proved something very similar is a good sign that you have been working on, and building up expertise in, a field of some importance. That means you are well-prepared to make a significant contribution. The fact that your approach was original is also a good sign. I would say that it's not so important that your approach happened to be not as good in this particular case; ultimately, originality is harder to come by and more valuable than whether you happen to beat out someone else's method in a particular instance.

Also, while it may feel that you are throwing everything in the bin and starting over from scratch, this is probably not accurate. What you have learned, and the thought processes you have had, are likely to have enduring value. It is common in one's career to go back and revisit old territory, and succeed in an area where one had previously failed. I vividly remember one example when I was a graduate student and failed to prove a certain conjecture. Someone else proved the conjecture soon afterward, and that was a deflating experience. But I came back to the problem later and proved a much more general result using an improved version of my old ideas.

In short, don't blow this setback out of proportion. Your efforts have probably been much less "wasteful" than you think. Everyone experiences similar setbacks, and you will surely bounce back as long as you are able to get your emotions under control.

Answer 3

It's really hard to say without more details as to what the field is, and how likely you are to be able to extend either your method, or the prior author's methods, to yield new results. Maybe you should try contacting the author in question to ask them what they think of your approach.

Another important question is how likely you are to be able to secure funding for one more year to work on your PhD. Since it often takes the better part of one year to learn the basics of a given field of math in order to make a research contribution, this time is not wasted anyway, but you will probably need some kind of extension. This, again, depends on many circumstances: ask other people in your lab / department / école doctorale what they think about it.

To summarize: it's certainly not good, but exactly how bad it is depends on the precise details of your situation.

Answer 4

I happen to have seen this post only a couple of hours after stumbling on a recollection by Bill Howard, from an article in the Mathematical Intelligencer written by Howard's student Amy Shell-Gellasch. (Howard went on to a quite distinguished career and is a fellow of the AMS.)

By the summer of 1951, I had been at Chicago for two years, and it was time that I got to work on a thesis. That summer Weil lived in a little monastic cell in International House, while his family went to France; so I encountered him almost daily at lunch or supper. One day he put down his tray and said, totally out of the blue, that he had a thesis problem for me. I suspect that there had been a faculty meeting, and they thought it was time Bill Howard was put to work.

This was a problem of Elie Cartan. Given one complex variable on a bounded domain, the group of one-to-one analytic mappings of that domain onto itself is a finite-dimensional Lie group. This group of all isometries in the space of constant negative curvature is the Poincare group. The elder Cartan generalized this to two and three complex variables. Namely, he showed that the underlying metric is "symmetric" in the sense that locally, reflection through a point by means of geodesics is an isometry. Weil said I should try to prove the result for the general case of n complex variables. And moreover, try to get a simple general proof for the case of two and three complex variables, so you wouldn't have to look at it case by case.

The way he told it to me, I assumed that Cartan had thought the theorem was true, and I think Weil thought the theorem to be true in general for n dimensions. I spent several months just acquiring the necessary background. I had to learn the theory of several complex variables, Lie groups, Riemannian geometry; it was too much. I was out of my depth but didn't know it. I had a good teacher for the geometry, Professor Chern.

By the spring of 1952 I thought I had solved the problem. I told Weil my proof and he thought it was okay. I presented it in a seminar; several high-powered Visiting mathematicians were there. They thought what I had done was reasonable; they couldn't check every detail in seminar, but they thought I was using the proper methods. Weil told me to write it up and submit it with a proof of Lemma 2, which lie was sure was true.

I went home, and as I was falling asleep, I was thinking of how I would write out the proof of Lemma 2. Then I realized that I couldn't prove Lemma 2. Then I noticed that there was a counterexample. Lemma 2 was false, so the whole thing imploded. I remember feeling that the bottom had physically fallen out of the bed. That was a real sinking feeling. The next day, I told Weil. He said, "What do you mean Lemma 2 is false!" I showed him my counterexample. He stormed out of the office. Ten minutes later he stormed back in and gave me his own counterexample.

He saw that I didn't look very happy, so he took me for a walk in Jackson Park. We walked along in silence for about ten minutes, and then he said, "Well, you've got enough results, bits and pieces, it's not what we had hoped. But you have enough there for a Ph.D. thesis, just write the bits and pieces up."

I guess he must have been serious, thinking about what I had already done, and there was enough there. I said I wanted it all or nothing. No bits and pieces for me.

We walked along in silence a little longer, and he said, "You have experience climbing mountains. You must know that you don't have to go to the top, to the peak. You can enjoy yourself going partway up. Just play around, you can see the other people going up."

You can imagine what I felt like at that point. He was trying to make it better. He was trying to put himself in my place, and he realized that he wouldn't have accepted it either. So what was coming out was sounding kind of strange.

Suddenly out of the blue, he said, "Have you ever thought of becoming an administrator?" That was a real inspiration to him. I told him that knowing what he thought about administrators, I considered that an insult. He said, "Take Walter Bartky" (who was the Dean of Physical Sciences). "Of course his mathematics is weak. But he's done some very worthwhile things."

I asked what he had done that was worthwhile. And Weil responded, "Well, he brought me here!"

Answer 5

Don't worry at all. At least for the first half of the thesis, you can present the work up to the point you're at now, and reference the literature as appropriate. Then, for the next stage of the thesis, present new extensions of what's been done.

If nothing you've done is original in a clear way right up to the end, I suppose either 1) given your approach may be slightly different, submit anyway and see what happens 2) keep working until you do have something totally original, since there is no real time limit you need to meet.

Publishing the research before submitting can help convince the examiners that what you've done is original, as the peer reviewers may regard it as substantially novel to merit publication, and if not I suppose that would lead you to the other path of carrying on researching for a bit.

I would say, which option you take depends on how big your field is. In many fields you can argue what you've done is essentially original and people will have to do a lot of work to prove its been done precisely that way before (and they usually don't have the time, even you didn't notice for years). In the worst case they just ask you to carry on with the thesis until you prove original research (one new paper probably).

Overall, having others working on the same problem can be advantage for the first half or so of the thesis as you can cite it as literature in the introduction, i.e. having no real link to existing work can be difficult when you write the thesis.

Answer 6

1. First, a positive aspect is that you were able to produce a relevant result which shows some maturity and mastering of a mathematical field.

2. Second, from what you say, it is not completely clear that what you found is not publishable. If your assumptions and conclusions are a bit different than in the other paper, but you have interesting cases where your results apply and not the other ones or where your conclusion give something stronger in some relevant cases. Also, if your method of proof is fundamentally different and can give rise to promising follow-up, this would be a positive point. Certainly you advisor will be able to determine whether what you have can be published and find a B plan if not. As say before, you gained a lot of experience from thinking and writing your result hence writing other papers will go more smoothly.

3. The research your did on this problem certainly rose new questions. It is possible that some research could be done on them. Of course, I do not know the field and the type of topic you worked on but your advisor certainly know, and this is his/her role.

4. Normally, your Ph.D. last three years and you can find a position of "Attaché Temporaire d'Enseignement et de Recherche" and defend during this supplementary year. So usually (and this is what I did), thesis last approximatively three years and two months : starting in September/October of the year n/(n+1), and defense in December of the year n+3, essentially in order to be on time to apply for the maître de conférence positions. With the overview you gained in your field and a supporting advisor, it is likely that you will have at least one or two submitted paper. It is not uncommon to not have yet accepted papers at the moment of writing the manuscript.

5. The progression in a Ph.D. is not linear, so you can do much more in the one year and half with the benefit of your experience than in the first two, which were by the way far from being unproductive.