<p>This is very common, and certainly frustrating. </p>

<p>Here is my advice: Don't wait until you have a complete result to start writing. Maintain a TeX document with formal descriptions of your problem, proofs of preliminary lemmas, etc. as you go. It is easy to convince yourself that something is true and overlook simple mistakes if you are holding the argument only in your head, but the process of writing something down formally forces you to find these mistakes. If you wait to write until the end, you might not find the mistake until you have already expended a lot of effort; if you write as you go, you can find the errors more quickly. </p>

CC BY-SA 3.0
2014-03-29T15:05:58.220Z
2014-03-29T15:05:58.220Z
Aaron Roth
<p>In <em><a href="http://en.wikipedia.org/wiki/How_to_Solve_It">How to Solve It</a></em>, Pólya advises:</p>

<blockquote>
  <p>"If you can't solve a problem, then there is an easier problem you can solve: Find it."</p>
</blockquote>

CC BY-SA 3.0
2014-07-15T01:16:10.437Z
2014-07-15T10:42:06.533Z
2014-07-15T10:42:06.533Z
Joseph O'Rourke
<p>There are some nice answers by others. I just want to add a few points:</p>

<ol>
<li><p>Don't panic! Usually, you expect to be graduated sooner than the average students because you think that you are smarter than most of them. Fast graduation doesn't mean you are better than others. Longer graduation time doesn't mean you are weaker that others. You are working on totally different problems. In some areas of computer science, this is enough to do a couple of experiment and write down the result, whatever it is, as a thesis. This is not true about the theory of CS.</p></li>
<li><p>Describe your problem and what you know about it in details to others. Ever if the audiences are not experts in your area, they may ask questions that turns on a light in your mind. Describing your problem forms a better understanding for yourself.</p></li>
<li><p>Attend various seminars, conferences, and courses, even if they look unrelated to your topic. Read related papers frequently. They will give you new ideas and clues to tackle the problem. Sometimes, it is difficult or impossible to solve the problem with the tools/methods that you have in mind. You need to find a new tool or idea to solve it.</p></li>
<li><p>Try to solve a simpler version of your problem first. Add new assumptions to simplify your problem or consider a special case. Once you solved the special case of the problem, you can relax the assumption or generalize the problem.</p></li>
<li><p>If you think that a portion of the problem is solvable, but you couldn't solve it, concentrate on that portion. Go to the library or somewhere that nobody disturbs you. Close your laptop. Turn off your cell phone. Focus on the problem for a few hours. Try it for a few times.</p></li>
</ol>

CC BY-SA 3.0
2014-03-30T10:02:46.647Z
2014-03-30T10:10:19.650Z
2014-03-30T10:10:19.650Z
Helium
<blockquote>
  <p>What do you do when you cannot make progress on the problem you have
  been working on?</p>
</blockquote>

<p>I go for a walk in the woods, or focus on something else for a while, and come back to the problem later.</p>

<blockquote>
  <p>Is this a common situation that a researchers notices that her idea is
  not going to work after considerable amount of work?</p>
</blockquote>

<p>Yes.  But as the accepted answer says, learn to test early and fail fast.</p>

<blockquote>
  <p>What do you do when you realized that an approach you had in mind is
  not going to work and the problem seems too difficult to solve?</p>
</blockquote>

<p>Talk to others about your work.  Get suggestions from them for other approaches you could pursue.</p>

<p>Primarily: talk to your supervisor, other lecturers, and peers in your department.</p>

<p>But beyond that, there are lots of other places to ask questions: newsgroups, mailing lists, web forums, and of course stackexchange sites.</p>

<blockquote>
  <p>What advice would you give to a student in my situation?</p>
</blockquote>

<p>Learn from your mistake, so that you won't make a similar mistake in the future.  Also share what you have learned with others, so they won't do the same!</p>

<p>I am sure it is very disappointing to be in this situation, but be encouraged by the knowledge that lots of other researchers have been here too, and have gone on to make progress with the problem.  Good luck to you!</p>

CC BY-SA 3.0
2014-03-30T08:51:52.953Z
2014-03-30T08:51:52.953Z
joeytwiddle
<ol>
<li>Don't panic.</li>
<li>Take a brief "vacation" from the problem to help clear any anxieties.</li>
<li>Read <a href="http://en.wikipedia.org/wiki/How_to_Solve_It" rel="nofollow">How to Solve It</a>.</li>
<li>Decide what will make you happier: retackle the problem or moving on to something new.</li>
<li>Whichever #4 fork you choose, remember you can always change your mind later.</li>
</ol>

CC BY-SA 3.0
2014-03-29T22:10:27.550Z
2014-03-29T22:10:27.550Z
joe snyder
<p>The higher quality the scientific research, <em>the harder it is</em> but also realize that early in ones career, one cannot realistically expect earth-shattering results (and not even later also!) You don't mention how you arrived at the problem you were given. Was it from an advisor? Did you come up with it yourself? If it came from elsewhere it's a lesson on fine-tuning/adjusting your personal discrimination/ parameters/ boundaries. Problem selection is critical. Don't "put all your eggs in one basket". If you are focused on one topic, look at multiple ways to work on it and multiple open problems in that area. Realize that <em>some problems cannot be solved and a big part of the game is developing a personal intuition on which ones can/can't</em>.</p>

<p>Scientific research is fundamentally <em>about the unknown</em>. Especially in TCS even experts routinely admit there are vast swathes of important unknown aspects &amp; even admit to personal frustration/disappointment on that. Look at the "big picture". Despite over a century old, TCS is still a rather young science. In many ways one could build a case and realize that TCS is <em>one of the hardest scientific fields</em> in existence among all scientific fields.</p>

<p>Try reading books/biographies about the historical greats in the field, they all struggled with serious research hardships and setbacks throughout their careers. We also are very lucky to have a very good picture of most of their lives. As <a href="http://www.einstein-website.de/z_kids/letterskids.html" rel="nofollow">Einstein said</a> <em>(in a letter to a child, but widely quoted &amp; taken to heart!)</em></p>

<blockquote>
  <p>Do not worry about your problems with mathematics, I assure you that mine are far greater.</p>
</blockquote>

<p>And of course there are highly accomplished experts/leaders who are alive right now and writing or even blogging about their research practices and careers! Blogs give an amazingly candid/ personal/ visceral snapshot of research-in-progress/motion that has never before been seen in scientific history. Again we're very lucky to have blogs and brilliant researchers who are willing to spend substantial time on them (this was not the case years ago and many scientists and professionals were justifiably reluctant to go into blogging). Two standouts in particular in TCS, <a href="http://rjlipton.wordpress.com/" rel="nofollow">RJLipton</a> and <a href="http://blog.computationalcomplexity.org/" rel="nofollow">Fortnow</a> blogs which both cover great behind-the-scenes verisimilitude. Another remarkable/inspiring story circulating recently is that of <a href="http://vzn1.wordpress.com/2013/10/04/zhang-twin-prime-breakthru-vs-academic-trackgrind/" rel="nofollow">Zhang</a>.</p>

<p>Make sure to socialize with your academic peers at conferences &amp; elsewhere (even somewhat on the internet if possible). You won't feel so alone, you'll see that struggle is an inherent part of the picture. Research is a fundamentally different activity than what precedes it in education, it's about a difficult/challenging shift from the known to <em>terra incognita</em>. The old adage written on centuries-old map regions prior to discovery of the "New World" still applies: <em>here there be dragons</em>.</p>

<p>Maybe somewhat synchronistically, here is a neat paper that has been circulating through many scientific blogs lately, it has caused quite an impact/stir, do a search to see all the reactions to it along the lines, <em>"wow isn't it great someone said that, how I've been feeling"</em>. Also am including some other refs that can be helpful in describing the picture.</p>

<ul>
<li><p><a href="http://jcs.biologists.org/content/121/11/1771.full" rel="nofollow">The importance of stupidity in scientific research</a> Schwartz. By a biologist but written in a general way such that other scientists from all fields are finding it insightful/compelling.</p></li>
<li><p><a href="http://rads.stackoverflow.com/amzn/click/B001949X9U" rel="nofollow">Idea factory: learning to think at MIT</a> by grad student White at MIT (mechanical engineering masters). At the end he describes his choice not to do a Phd based on his experiences/challenges.</p></li>
<li><p><a href="http://rads.stackoverflow.com/amzn/click/B004EHZDE8" rel="nofollow">A PhD is not enough: a guide to survival in science</a> Feibelman. Shows an accurate picture of building a career and how the Phd degree is really just the very beginning. Some describe it as a "union card/ work permit"!</p></li>
</ul>

CC BY-SA 3.0
2014-03-29T15:00:12.810Z
2016-04-29T23:13:51.353Z
2016-04-29T23:13:51.353Z
vzn
<p>Here's a question to ponder: why turn to a public forum composed of people who know nothing about the specifics of your situation when you're supposed to have an academic adviser precisely to handle such questions! Don't get me wrong, you got some great tips here (and meta-tips), but ultimately it's precisely during such crises that one turns to one's mentor for guidance.</p>

<p>The real question at this point, I think, is not whether or not to leave grad school, but rather: Is this still a good problem for a PhD student? Should I seek a less challenging result at this point? Or perhaps change directions? These are the <em>substantive</em> questions I'd be posing -- and not to unfamiliar (even if good-intentioned) strangers, but rather to people better acquainted with my specific case (such as, ahem, the adviser!).</p>

<p>PS I understand that not everyone is blessed with an approachable, supportive adviser. I would invest serious effort in trying to find one. This PhD journey is hard enough <em>with</em> good guidance.</p>

CC BY-SA 3.0
2016-05-01T14:54:23.560Z
2016-05-01T14:54:23.560Z
Aryeh
<blockquote>
  <p>Is this a common situation that a researchers notices that her idea is
  not going to work after considerable amount of work?</p>
</blockquote>

<p>Yes. But as you get more experienced, you're able to "fail fast" - learn how to test the idea quickly to see if it passes a 'smell test'. </p>

<blockquote>
  <p>What do you do when you realized that an approach you had in mind is
  not going to work and the problem seems too difficult to solve?</p>
</blockquote>

<p>It depends. Sometimes the best thing to do is put the problem away for a while and work on something else. Sometimes the failure suggests a different question. </p>

<blockquote>
  <p>What advice would you give to a student in my situation?</p>
</blockquote>

<p><img src="https://i.sstatic.net/rLg5o.png" alt="enter image description here"></p>

CC BY-SA 3.0
2014-03-29T08:08:44.263Z
2014-03-29T08:08:44.263Z
Suresh Venkat
<p>I am a 2nd year graduate student in theory.
I have been working on a problem for the last year (in graph theory/algorithms).
Until yesterday I thought I am doing well (I was extending a theorem from a paper).
Today I realized that I have made a simple mistake. 
I realized that it will be much harder than I thought to do what I intended to do. 
I feel disappointed so much I am thinking about leaving grad school.</p>

<p>Is this a common situation that a researchers notices that her idea is not going to work after considerable amount of work?</p>

<p>What do you do when you realized that an approach you had in mind is not going to work and
the problem seems too difficult to solve?</p>

<p>What advice would you give to a <em>student</em> in my situation?</p>

CC BY-SA 3.0
2014-03-28T20:33:13.030Z
Most people go through the same crisis at about the same time. If you work hard on your failures, they're teaching you more than you realize.
Sasho Nikolov
CC BY-SA 3.0
2014-03-29T04:03:50.040Z
If you don't spend almost all of your time feeling like an idiot, you're not really doing research.
Jeffε
CC BY-SA 3.0
2014-03-29T14:03:05.423Z
Don't underestimate the value of life-work balance --- taking a break to do something fun with friends or spend time on a hobby or so on.
usul
CC BY-SA 3.0
2014-03-29T15:49:11.303Z
See [How should I deal with discouragement as a graduate student?](http://academia.stackexchange.com/q/2219/6318)
Juho
CC BY-SA 3.0
2014-03-29T16:00:29.343Z
Write code to enumerate your complexity exactly. The mere act of writing the code leads you to formalize everything you may have hand waived.
Chad Brewbaker
CC BY-SA 3.0
2014-03-29T16:31:15.117Z
Something else: keep talking to people about your research, and work on a few things at a time, so that you can switch gears when you get stuck with something.
Sasho Nikolov
CC BY-SA 3.0
2014-03-29T18:53:05.253Z
try formulating it as a stackexchange question! win/win either way, if theres an answer it could be a research lead & if there are no answers then you can confirm your intuition its hard... also have found that empirical research can lead to many ideas/insights... and by the way like any other field _research is not for everyone_ and its not a unmitigated disaster to admit that...
vzn
CC BY-SA 3.0
2014-03-29T19:21:59.430Z
It is generally a good idea to work on a couple of things at the same time. Second, even if the main project fails it may be possible to salvage some thing out of the ideas. It comes more easily with experience and you should not hesitate to ask your advisor for help.
Chandra Chekuri
CC BY-SA 3.0
2014-03-30T09:21:52.787Z
"What do you do when you realized that an approach you had in mind is not going to work and the problem seems too difficult to solve?"

Repeat 100 times: try another approach.
If that fails, then Repeat 100 times: try another problem.  Hope that you can see how important "fast fail" is.
Noam
CC BY-SA 3.0
2014-03-31T13:01:55.307Z
Learning why the hard problem is actually hard is valuable knowledge. Also, note that your situation doesn't go away if you, say, go into industry instead of academia; it gets far worse. Whole teams of people working for years on software that never ships is common. Its discouraging, but part of taking risks is being willing to suffer setbacks.
Eric Lippert
CC BY-SA 3.0
2016-05-01T01:54:17.887Z
Just make your repository public. See Brent's: https://github.com/byorgey/thesis Or mine: https://github.com/chadbrewbaker/endoscope Ask those in your area to look it over. Feel free to pick my brain about your project (that goes for anybody). Combinatorialist by trade, I often see algebraic data structures where others see algorithms. Might give you a fresh point of view.
Chad Brewbaker
<soft-question><research-practice>
What do you do when you cannot make progress on the problem you have been working on?
Kumar
# What do you do when you cannot make progress on the problem you have been working on?

(Asked by: username_0 on 2014-03-28)

I am a 2nd year graduate student in theory.
I have been working on a problem for the last year (in graph theory/algorithms).
Until yesterday I thought I am doing well (I was extending a theorem from a paper).
Today I realized that I have made a simple mistake.
I realized that it will be much harder than I thought to do what I intended to do.
I feel disappointed so much I am thinking about leaving grad school.

Is this a common situation that a researchers notices that her idea is not going to work after considerable amount of work?

What do you do when you realized that an approach you had in mind is not going to work and
the problem seems too difficult to solve?

What advice would you give to a *student* in my situation?

**Tags:** soft-question, research-practice

> **Comments:**
> **username_1**: Most people go through the same crisis at about the same time. If you work hard on your failures, they're teaching you more than you realize.  
> **username_2**: If you don't spend almost all of your time feeling like an idiot, you're not really doing research.  
> **username_3**: Don't underestimate the value of life-work balance --- taking a break to do something fun with friends or spend time on a hobby or so on.  
> **username_4**: See [How should I deal with discouragement as a graduate student?](http://academia.stackexchange.com/q/2219/6318)  
> **username_5**: Write code to enumerate your complexity exactly. The mere act of writing the code leads you to formalize everything you may have hand waived.  
> **username_1**: Something else: keep talking to people about your research, and work on a few things at a time, so that you can switch gears when you get stuck with something.  
> **username_6**: try formulating it as a stackexchange question! win/win either way, if theres an answer it could be a research lead & if there are no answers then you can confirm your intuition its hard... also have found that empirical research can lead to many ideas/insights... and by the way like any other field _research is not for everyone_ and its not a unmitigated disaster to admit that...  
> **username_7**: It is generally a good idea to work on a couple of things at the same time. Second, even if the main project fails it may be possible to salvage some thing out of the ideas. It comes more easily with experience and you should not hesitate to ask your advisor for help.  
> **username_8**: "What do you do when you realized that an approach you had in mind is not going to work and the problem seems too difficult to solve?"  Repeat 100 times: try another approach. If that fails, then Repeat 100 times: try another problem.  Hope that you can see how important "fast fail" is.  
> **username_9**: Learning why the hard problem is actually hard is valuable knowledge. Also, note that your situation doesn't go away if you, say, go into industry instead of academia; it gets far worse. Whole teams of people working for years on software that never ships is common. Its discouraging, but part of taking risks is being willing to suffer setbacks.  
> **username_5**: Just make your repository public. See Brent's: https://github.com/byorgey/thesis Or mine: https://github.com/chadbrewbaker/endoscope Ask those in your area to look it over. Feel free to pick my brain about your project (that goes for anybody). Combinatorialist by trade, I often see algebraic data structures where others see algorithms. Might give you a fresh point of view.  

---

## 8 answers

### Answer by username_16 on 2014-03-29. Score: 52 | Accepted answer

> Is this a common situation that a researchers notices that her idea is
> not going to work after considerable amount of work?

Yes. But as you get more experienced, you're able to "fail fast" - learn how to test the idea quickly to see if it passes a 'smell test'.

> What do you do when you realized that an approach you had in mind is
> not going to work and the problem seems too difficult to solve?

It depends. Sometimes the best thing to do is put the problem away for a while and work on something else. Sometimes the failure suggests a different question.

> What advice would you give to a student in my situation?

![enter image description here](https://i.sstatic.net/rLg5o.png)


---

### Answer by username_10 on 2014-03-29. Score: 40

This is very common, and certainly frustrating.

Here is my advice: Don't wait until you have a complete result to start writing. Maintain a TeX document with formal descriptions of your problem, proofs of preliminary lemmas, etc. as you go. It is easy to convince yourself that something is true and overlook simple mistakes if you are holding the argument only in your head, but the process of writing something down formally forces you to find these mistakes. If you wait to write until the end, you might not find the mistake until you have already expended a lot of effort; if you write as you go, you can find the errors more quickly.


---

### Answer by username_11 on 2014-07-15. Score: 10

In *[How to Solve It](http://en.wikipedia.org/wiki/How_to_Solve_It)*, Pólya advises:

> "If you can't solve a problem, then there is an easier problem you can solve: Find it."


---

### Answer by username_12 on 2014-03-30. Score: 7

There are some nice answers by others. I just want to add a few points:

1. Don't panic! Usually, you expect to be graduated sooner than the average students because you think that you are smarter than most of them. Fast graduation doesn't mean you are better than others. Longer graduation time doesn't mean you are weaker that others. You are working on totally different problems. In some areas of computer science, this is enough to do a couple of experiment and write down the result, whatever it is, as a thesis. This is not true about the theory of CS.
2. Describe your problem and what you know about it in details to others. Ever if the audiences are not experts in your area, they may ask questions that turns on a light in your mind. Describing your problem forms a better understanding for yourself.
3. Attend various seminars, conferences, and courses, even if they look unrelated to your topic. Read related papers frequently. They will give you new ideas and clues to tackle the problem. Sometimes, it is difficult or impossible to solve the problem with the tools/methods that you have in mind. You need to find a new tool or idea to solve it.
4. Try to solve a simpler version of your problem first. Add new assumptions to simplify your problem or consider a special case. Once you solved the special case of the problem, you can relax the assumption or generalize the problem.
5. If you think that a portion of the problem is solvable, but you couldn't solve it, concentrate on that portion. Go to the library or somewhere that nobody disturbs you. Close your laptop. Turn off your cell phone. Focus on the problem for a few hours. Try it for a few times.


---

### Answer by username_13 on 2014-03-30. Score: 3

> What do you do when you cannot make progress on the problem you have
> been working on?

I go for a walk in the woods, or focus on something else for a while, and come back to the problem later.

> Is this a common situation that a researchers notices that her idea is
> not going to work after considerable amount of work?

Yes. But as the accepted answer says, learn to test early and fail fast.

> What do you do when you realized that an approach you had in mind is
> not going to work and the problem seems too difficult to solve?

Talk to others about your work. Get suggestions from them for other approaches you could pursue.

Primarily: talk to your supervisor, other lecturers, and peers in your department.

But beyond that, there are lots of other places to ask questions: newsgroups, mailing lists, web forums, and of course stackexchange sites.

> What advice would you give to a student in my situation?

Learn from your mistake, so that you won't make a similar mistake in the future. Also share what you have learned with others, so they won't do the same!

I am sure it is very disappointing to be in this situation, but be encouraged by the knowledge that lots of other researchers have been here too, and have gone on to make progress with the problem. Good luck to you!


---

### Answer by username_14 on 2014-03-29. Score: 3

1. Don't panic.
2. Take a brief "vacation" from the problem to help clear any anxieties.
3. Read [How to Solve It](http://en.wikipedia.org/wiki/How_to_Solve_It).
4. Decide what will make you happier: retackle the problem or moving on to something new.
5. Whichever #4 fork you choose, remember you can always change your mind later.


---

### Answer by username_6 on 2014-03-29. Score: 2

The higher quality the scientific research, *the harder it is* but also realize that early in ones career, one cannot realistically expect earth-shattering results (and not even later also!) You don't mention how you arrived at the problem you were given. Was it from an advisor? Did you come up with it yourself? If it came from elsewhere it's a lesson on fine-tuning/adjusting your personal discrimination/ parameters/ boundaries. Problem selection is critical. Don't "put all your eggs in one basket". If you are focused on one topic, look at multiple ways to work on it and multiple open problems in that area. Realize that *some problems cannot be solved and a big part of the game is developing a personal intuition on which ones can/can't*.

Scientific research is fundamentally *about the unknown*. Especially in TCS even experts routinely admit there are vast swathes of important unknown aspects & even admit to personal frustration/disappointment on that. Look at the "big picture". Despite over a century old, TCS is still a rather young science. In many ways one could build a case and realize that TCS is *one of the hardest scientific fields* in existence among all scientific fields.

Try reading books/biographies about the historical greats in the field, they all struggled with serious research hardships and setbacks throughout their careers. We also are very lucky to have a very good picture of most of their lives. As [Einstein said](http://www.einstein-website.de/z_kids/letterskids.html) *(in a letter to a child, but widely quoted & taken to heart!)*

> Do not worry about your problems with mathematics, I assure you that mine are far greater.

And of course there are highly accomplished experts/leaders who are alive right now and writing or even blogging about their research practices and careers! Blogs give an amazingly candid/ personal/ visceral snapshot of research-in-progress/motion that has never before been seen in scientific history. Again we're very lucky to have blogs and brilliant researchers who are willing to spend substantial time on them (this was not the case years ago and many scientists and professionals were justifiably reluctant to go into blogging). Two standouts in particular in TCS, [RJLipton](http://rjlipton.wordpress.com/) and [Fortnow](http://blog.computationalcomplexity.org/) blogs which both cover great behind-the-scenes verisimilitude. Another remarkable/inspiring story circulating recently is that of [Zhang](http://username_61.wordpress.com/2013/10/04/zhang-twin-prime-breakthru-vs-academic-trackgrind/).

Make sure to socialize with your academic peers at conferences & elsewhere (even somewhat on the internet if possible). You won't feel so alone, you'll see that struggle is an inherent part of the picture. Research is a fundamentally different activity than what precedes it in education, it's about a difficult/challenging shift from the known to *terra incognita*. The old adage written on centuries-old map regions prior to discovery of the "New World" still applies: *here there be dragons*.

Maybe somewhat synchronistically, here is a neat paper that has been circulating through many scientific blogs lately, it has caused quite an impact/stir, do a search to see all the reactions to it along the lines, *"wow isn't it great someone said that, how I've been feeling"*. Also am including some other refs that can be helpful in describing the picture.

* [The importance of stupidity in scientific research](http://jcs.biologists.org/content/121/11/1771.full) Schwartz. By a biologist but written in a general way such that other scientists from all fields are finding it insightful/compelling.
* [Idea factory: learning to think at MIT](http://rads.stackoverflow.com/amzn/click/B001949X9U) by grad student White at MIT (mechanical engineering masters). At the end he describes his choice not to do a Phd based on his experiences/challenges.
* [A PhD is not enough: a guide to survival in science](http://rads.stackoverflow.com/amzn/click/B004EHZDE8) Feibelman. Shows an accurate picture of building a career and how the Phd degree is really just the very beginning. Some describe it as a "union card/ work permit"!


---

### Answer by username_15 on 2016-05-01. Score: 1

Here's a question to ponder: why turn to a public forum composed of people who know nothing about the specifics of your situation when you're supposed to have an academic adviser precisely to handle such questions! Don't get me wrong, you got some great tips here (and meta-tips), but ultimately it's precisely during such crises that one turns to one's mentor for guidance.

The real question at this point, I think, is not whether or not to leave grad school, but rather: Is this still a good problem for a PhD student? Should I seek a less challenging result at this point? Or perhaps change directions? These are the *substantive* questions I'd be posing -- and not to unfamiliar (even if good-intentioned) strangers, but rather to people better acquainted with my specific case (such as, ahem, the adviser!).

PS I understand that not everyone is blessed with an approachable, supportive adviser. I would invest serious effort in trying to find one. This PhD journey is hard enough *with* good guidance.


---

