I am a second year Ph.D. student in a North American university who is mostly working on applied mathematics with a supervisor/advisor/PI. I have been troubled by a pattern of my own behaviour that seems to go against the seemingly correct way to succeed in research and I wonder if I have some sort of an "anti-research" personality.

Here are the problems:

  1. I study whatever is interesting and cool (within a reasonable range of my discipline) and this causes me to lack a solid focus. It seems to me that people who wind up obtaining a PhD learn to abandon so-called academic freedom early on and drill into a tiny research area. For example, while other people's research could be about different types of seahorses, my research would be about seahorses, pipe fish, shrimps...you get the picture.

  2. Since I work in applied math, therefore I often demand more proof of applicability, where my supervisor is totally happy with toy models. He thinks it is completely sufficient for publishing a paper while I think it is fake applied research. This seems to generate some conflict between us and usually I am the one who gives in at the end and do some simulation on these toy models to make him happy - I never care about these problems. Most other people in my field only simulate toy models as well, not really "real-world" applicable in any sense, but hey, it is sure pumping out a lot of papers.

  3. I never collaborate or ask for help from my peers no matter how stuck I become. I often see my colleagues collaborate with each other in the office. A part of me is jealous that they are taking advantage of each other's knowledge, another part of me almost thinks that this is like cheating. I feel that my thesis and my ideas wouldn't be mine if it was interfered or influenced this way. It wouldn't feel authentic

  4. I move on to a completely new topic immediately after I finish my old one. Usually the way I see how other people work is that they try to do something tangentially similar to what they have done before, i.e., blue-tailed seahorses, then yellow-tailed seahorses. I jump to studying pipe fish immediately after I warp up my research on seahorses. I think my advisor must dislike me immensely for starting from scratch after every project.

  5. If a problem seems to have an easy or existing approach that solves it, I find the problem less attractive to the point that I get physically sick from reading about other people's approach. However, a lot of times in research I find that other people would simply adapt other people's method for their own problem and then publish a paper that way. I try to solve it in my own way every time and most of the times it gets to a point where my supervisor intervenes and tell me to do whatever other people are doing. Again, I give in at the end.

  6. I don't even try to follow my advisor's vision of my project. My advisor seems to have his own vision and ulterior goals that are not completely aligned with mine. I think a good PhD student should just listen to him like a father-figure and do whatever I am told. But I don't agree or sometimes don't even care about his specific vision. For example, why should I do a research on the dorsal fin of a seahorse (for your "dorsal fin grant") when I can study pipe fish instead? I understand that he is the one who is funding me, but I also care deeply about my own academic freedom.

Given these habits, am I doomed to fail my PhD? Do I have an anti-research personality?

  • 74
    "I get physically sick from reading about other people's approach." This is a pretty striking thing to say and suggests something deeper is going on. You come across as rather hostile to people in general, which is going to make things tricky in any career. Commented Apr 26, 2019 at 15:32
  • 49
    Honestly? It sounds like you prefer "problem-solving" to research and would probably be happier in industry than academia. Commented Apr 26, 2019 at 18:26
  • 9
    "1. ... It seems to me that people who wind up obtaining a PhD learn to abandon so-called academic freedom early on and drill into a tiny research area." I can't speak for what type of maths you're doing, but I do pure maths (discrete probability), and this is not what happens. Sure, I specialise in a particular field, but it's not like I just do one thing the whole time. My supervisor has worked on stuff to do with Brownian motion, BitTorrent algorithms, percolation, random walks, random graphs -- and I would say her research is quite narrow compared with some!
    – Sam OT
    Commented Apr 26, 2019 at 21:37
  • 3
    Maybe you actually have got a personality which is averse to some parts of how research is practiced at certain institutions ;) but if you pay attention to stay diplomatic, that does absolutely not mean you are doomed to fail. (Please remember, there is a large social component in doing a PhD, no matter what the technical regulations say.)
    – jvb
    Commented Apr 26, 2019 at 22:26
  • 5
    @Elizabeth Really? Someone who wants to work on their own, can't follow direction from their boss (good luck with that) and doesn't see value in iteratively improving things should prefer working in the industry? Each one of those seems like a showstopper to me.
    – Voo
    Commented Apr 28, 2019 at 17:20

7 Answers 7

  1. Having a broad set of interests and knowledge is fine, and can lead to some 'outside of the box' solutions. Yes, you will find periods where anything else is more interesting than your PhD work, irrespective of how interesting your PhD work actually is. You'll find that as you come closer to the end of your PhD, your concentration on the problem at hand will sharpen, and while a PhD deadline isn't quite as good at sharpening a mind as an impending duel, you probably will find your ability to concentrate improve as the ending comes into sight.

    Furthermore, don't assume what you're researching your PhD on is what you'll be doing for the rest of your life. Having a wide set of skills and a shallow knowledge of many things will often help you out when you (most likely) realise you don't have the desire to become an academic, and need to search for a different job (which, let's face it, given your background means probably going in to Data Science)

  2. I don't know too much about the culture of applied math to make an informed comment on this, but in general, finding a good real-world application of a concept, and carrying it out, is difficult. It can involve a lot of time mucking around with real world datasets, which are often messy. You have an obligation to show that your results and methods are useful, but to what degree is up to taste, and I don't think is an issue with any kind of 'anti-research' personality.

  3. This sort of thinking is by far your most serious problem. If asking fellow students for help and collaborating is cheating, then so is using Stackexchange or reading from a textbook. Modern civilisation rests on the ability to record our thoughts so every human doesn't have to derive all the rules from scratch. There is nothing dishonourable about asking for help. If someone gives you helpful ideas, thank them in your thesis. Even if they do clever novel work on your problem, you still have to at the very least understand it and synthesize it into your own work.

    There is a certain kind of person who is reluctant to ask questions. I would count myself as one. If you feel uncomfortable doing do, I recommend working on that skill until you do feel more comfortable. Stackexchange is the perfect place for that - even if it isn't a question about anything to do with your research.

  4. This behaviour is fine. One can get a certain fatigue when working on certain projects for a while.

  5. & 6. It does really seem like you have a need to derive and understand everything from its foundations. In real life, this is rarely necessary.

    I did a PhD in organic chemistry. After that, I decided I didn't like chemistry anymore and went on to be a Data Scientist. At first, I would spend a lot of time trying to mathematically understand the techniques I was using, and I wouldn't feel comfortable using them if I didn't understand the underlying linear algebra. Then I slowly got more comfortable using techniques whose underlying mechanics I don't understand. We by and large don't understand the inner workings of a car or computer. We do know, roughly, its outputs when given certain inputs. The inner workings are a problem already solved by someone else.

    As you grow older and read more, you'll be continuously struck by the sheer quantity of stuff out there that people have figured out. The sheer amount of knowledge that goes into, say, building an aeroplane or a computer game or a treatment plan for a specific disease or a skyscraper or a hadron collider. Letting go of the need of having to understand all aspects of a certain thing is an important skill. Practice triage with the information you receive and the problems you encounter. Trust in the expertise of others who have come before you. Know when to expend your brainpower, and know when to conserve it.

So in summary, apart from issue 3, I don't think you have any significant "anti-research' personality issues.

  • 18
    To add to issue 3, the academic world relies heavily on networking and collaborations are a key element of that. Even if it is just a short chat about common research interests over a cup of coffee, people are much more likely to remember you and your research if you work with them. And if no one knows you, your papers are far less likely to be read and people will far less likely consider you when they have open positions to fill or grants to give.
    – mlk
    Commented Apr 26, 2019 at 7:57
  • 9
    Agree. To further point 3, I find it helpful during a brainstorming period to sit and talk through the problem with someone else. Having to formulate the problem in words understood by someone else helps me actually understand it too. Much like you don’t really understand your results until you write the paper such that someone else can too.
    – Jon Custer
    Commented Apr 26, 2019 at 13:29
  • 2
    I, Pencil — youtube.com/watch?v=IYO3tOqDISE — lots of effort goes into even the simplest things.
    – jmoreno
    Commented Apr 27, 2019 at 4:53
  • Good, thorough answer. The only thing I’d add is that if you struggle to ask good questions, start by trying to answer the questions of others. Other people may well provide the perfect "real world" problems that you (the OP) crave, and if you can give them a good explanation of the method, you don’t have to go through the "boring" fine details of implementation and thorough evaluation.
    – Pam
    Commented Apr 28, 2019 at 20:02

Let me preface my answer by challenging an unwritten assumption of yours: that you have a fixed "personality" which is hampering your potential as a researcher. This simply is false. Nobody is born a good researcher. It takes hard work to become one. Sure, some people have predispositions that help them. But in the end, you cannot avoid doing the work, including work on yourself.

You have discovered that you lack certain skills, or that your aptitude for them is currently insufficient. Blaming this on your personality as something that you cannot change is lazy. It is up to you to improve in these areas. If you refuse, then you are to blame, not some god-given "personality" that was forced upon you.

I will now answer point by point, but if you are honest with yourself, you already know what I am going to say.

  1. There is a common saying: "jack of all trades, master of none". In math, you are studying concepts that other people have been studying and refining for decades if not centuries. You are not going to master them by studying them for a few months and moving on to the next target. You are now at the bleeding edge of research, and it takes hard work to get up to speed. Your PhD is the occasion that you get to demonstrate that you are able to become a true expert at something and make improvements to the state of the art. It is unlikely that you will manage that by working on something for six months and moving on to something else afterwards.
    However, getting interested in other things is not just fine, it is mandatory if you want to have a successful career after your PhD.
  2. You seem to be confused about what applied math really is. Math that you actually apply in the real world is usually called engineering. It is a one-in-a-million occurrence for something in applied math to find a real-world application. But since you don't know in advance what will work, you have to start somewhere. Toy models are where it's at. You start with something simple. Maybe it works. Maybe you realize it's more complicated than what it appeared (the most common occurrence). Maybe it turns out to be useless. You don't know, because you are not an oracle.
  3. There is nothing "fake" about getting influenced by others. Here is another common saying: in academia, we are standing on the shoulders of giants. You are reading papers, aren't you? You didn't discovered all of applied math by yourself from scratch, did you? Aren't these papers influencing your research, your way of thinking? Have you never read something and thought, "hey, I never thought about it like that", or "wow, this unrelated topic gave me ideas for my current research"? The difference with face to face conversations is that it's happening in real time. That's basically it.
    And here's another saying, as I like them: alone you go faster, together you go farther. Other people have a different way of thinking, a different skillset, a different knowledge of the literature, different ideas. By pooling your resources together, you will probably be able to solve bigger problems than if you were on your own.
    Finally, collaborating is just fun. Try it and you will see.
  4. See #1. If you are happy with making tiny contributions to the state of the art all the time, good for you. (This is especially at odds with your apparent disgust for people who "pump out" papers, but whatever.) Meanwhile, someone will study seahorses for ten years and revolutionize the field by realizing that seahorses are aquatic poneys, rendering most of your previous research mostly useless.
  5. Solving things on your own is fine and valuable. Being able to use other people's ideas to solve your problem more quickly is an extremely valuable skill, however. While you will be reinventing the wheel, others will go around the world in a plane.
  6. This is something between you and your advisor. As a PhD student, you are supposed to transition from supervised research to autonomous research. If you really feel this way, talk about it openly with your supervisor. Maybe you will be surprised. Maybe your supervisor even thinks that you are not ready for unsupervised research because of your other points (unability to focus, to collaborate, to make use of other people's ideas and applying them to your own problem…) and this is why he is still asking you to work on something where he can directly help you and direct you in your research, instead of letting you work on something with less direction and help.

So yes, if you continue with the mindset that there are certain things about yourself that you cannot improve due to your "personality", you will have a hard time, in academia and elsewhere. You will continue to give up at the first obstacle and never amount to much. And you can continue to think that nature, your personality, your upbringing… is to the culprit, in the end, you are the one who has to live with the consequences.

  • 6
    Just adding some nuance to your statement that "Nobody is born a good researcher.". I think it's the opposite: everyone is born a researcher. Observing babies shows that they are excellent experimental scientists: they will keep trying to do whatever it is they are interested in until they figure it out, then move on to the next interesting thing, etc. It's too bad that we lose this ability at some point in late childhood and have to learn it again later on if we want to become good at doing research.
    – Guillaume
    Commented Apr 26, 2019 at 17:16
  • 3
    I'm on @user108161 's side on this: I guess the "natural" thing in everyday life is jumping to conclusions - that's the way selection works: most of the time, our conclusions and preconceptions either hold or are at least (computationally) cheap. Handling (understanding, modelling) counterintuitive relations usually needs some advanced training.
    – jvb
    Commented Apr 26, 2019 at 22:14

Short answer to complement other longer good ones here.

You do seem really to care about the seahorses of all colors, and the pipefish and the shrimp. So focus now on learning whatever you can in your current environment. Continue reading stuff that's not directly applicable. Do collaborate. Finish your PhD (toy models are sometimes good places to start). Then look for a postdoc with someone whose philosophy and style better match yours. When you run your own lab, look for students like you.

  • @SquaringtheCircleisEasy Thank you for the (unexpected!) bonus. When you're ready you might enjoy contacting my son (web page a little out of date): ms.mcmaster.ca/~bolker Commented May 4, 2019 at 20:43

“Try to learn something about everything and everything about something.”—Thomas Huxley.

Obtaining a doctorate is much more about the second aim than the first. Your advisor understands the practicalities of this, given the finite limits of time, human ability, and other resources.

I sympathize with you, in that I like to study what interests me—occasionally drilling down deeply when I come across something really interesting and sometimes jumping off to look at something different. Thus I am quite unsuited to studying for a doctorate, as perhaps you are.

You can't have it both ways. Either knuckle down and take your supervisor's advice, for a chance of getting a PhD, or follow your nose (as I would do). Another quote from Thomas Huxley:

“Make up your mind to act decidedly and take the consequences. No good is ever done in this world by hesitation.”


The only problem is the issue you have about networking/collaboration. There are different styles of research and approaches, not everyone "processes" things in the same way. Having a large survey level knowledge of the field is actually very important and its a skill that often some people don't have. I recommend to acquire professional level skills on something practical and useful across fields (programming, probability, numerical methods) and then you can always apply that skillset to different problems.


From a research psychologist: there is no anti-research personality. You did a good job identifying various barriers to specific goals, such as completing your PhD. It's up to you whether those goals are worth adjusting the approach to the barriers, either through behavior modification or changes in how you view the problems, e.g., through cognitive behavioral therapy. Such a practice would be helpful to most anyone, regardless of their mental health status. Reading your whole question carefully, it sounds like there are two struggles: 1) not meeting your expectations of concrete goals, and 2) managing negative feelings that might secondarily impede your goals (and reduce your quality of life in the process). It might be worth considering what strategies could help you continue to make constructive progress with understanding your approaches and likely outcomes. You're already doing a good job on this path by asking these questions.


Few small points about 2 and 5.

2) Toy models probably are often applicible as an inspritation. For example, say you want to change the whole US college admission methodology to better. There is a model for that, i.e. Stable Marriage Problem. Is it applicable directly? No. No one can make a preference list of all schools that one is interested in. But you can apply it in some sense. You can make all the applicants to make a small list, maybe with 10 schools each, and then you can proceed with the ordinary prosedure. What the "toy model" teaches us is that this process is stable if everyone lists every school in order based on desire. Increasing the list length will make it more likely to get everyone in a stable matching.

5) I will only adress a small part of this as it has many issues. It is completely fine to start from scratch ignoring all the previous research. I have heard a similar anectod concerning a famous mathematician. It turns out, when starting on a problem that researcher would ignore all the previous research and would try to solve it by himself for a while. If he fails to make it work then he would read the literature. I don't think there is something inherently wrong with tring to work on the problem without reading others'. The issue with what you say starts, as pointed out by others, when you don't want to read others' work no matter what.

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