Some areas that come to mind:
theory of partial differential equations (analysis and pdes, not numerical PDE)
number theory
algebra
Should I pick a trendy topic so that it is "easier" to write a thesis?
I've heard from senior PhD students not to try and write a thesis on analysis of PDEs because so much has already been done in this field and so it's very hard to do something new.
If you pick an overly-trendy area there is a chance that it will be easier to get a Ph.D. in that area but that many mathematicians will be less than impressed by the resulting degree. For example, "fuzzy" is (or has been?) a trendy concept. There is almost a template for getting a Ph.D. in it (albeit one which is getting harder to apply by sheer competition): pick some topic in pure mathematics for which there doesn't yet exist a fuzzy version (for an example the exact phrase "fuzzy symmetry group" has only 4 Google hits). Learn the classical theory. Fuzzify it: whenever you see the word "set" replace it with "fuzzy set". Prove something -- which with lack of competition shouldn't be all that hard. Anticipating the question as to why anyone should care, hand-wave about potential applications to artificial intelligence. Voila! You have a dissertation (I am exaggerating a bit, this is of course easier said than done, and a successful fuzzification will involve more than simply replacing sets by fuzzy sets).
Now I don't deny that the core concepts of fuzzy logic and fuzzy set theory have a great deal of mathematical depth, and that much of the fuzzification of classical pure mathematics has been well-motivated. Still, it seems likely that much of it has been done just because it was low-hanging fruit for somebody who wanted to write a dissertation or paper. I am instinctually skeptical of the value of a paper when it contains the word "fuzzy" in the title. I won't dogmatically reject it, but I will need some convincing as to its value. If your dissertation has a trendy buzz-word but otherwise seems unmotivated, you might meet with similar skepticism.
All of the areas you mention are extremely broad areas and extremely popular. For instance, it doesn't make sense to call number theory a trendy topic or not, except in the sense that there are many trends that come and go within number theory. Moreover, being "trendy" is essentially independent of being "relatively easy." Two topics that are sort of trendy in number theory close to me now are p-adic Langlands and beyond endoscopy, both of which are incredibly technical and require a huge amount of background to get into, whereas some other trendy parts of number theory like Apollonian circle packings and Ramanujan graphs are much easier to get into.
Just because a certain subject is more established doesn't mean it's harder to work in. It just means it's richer and has more subareas to specialize in.
What you should do your thesis is an area that (1) you would be happy working in, and (2) you can find a suitable advisor for. In any case, easy should not be a reason for doing a PhD (most people will tell you it is not easy---mine turned out to be, but I got lucky).
Note: there are certain areas that have fallen out of favor, and it can be harder to get an academic research position if you work in one of these areas, unless you can connect it to things people are interested in nowadays. However, there's a big difference between not being trendy and being comatose.
I'm going to say some stuff based on my own Physics PhD. Disclaimer: These are just my opinions and are undoubtedly affected by my cynicism.
PhDs are not all created equal
I'm of the belief that PhDs are not equally difficult. Additionally, PhDs are not equally valuable. In fact, value does not necessarily correlate with difficulty. I knew students who were given projects that turned out to be gifts - a simple idea with simple execution that produced papers like a gold mine. Some PhD projects are absolutely easier than others so don't let anyone persuade you otherwise.
Myself, I got landed with something that was borderline impossible (professors from other labs expressed their sympathies when I described my work) and, though I eventually succeeded, trying to get scientific value out of it was like trying to get blood out of a stone.
Here's my advice:
That's it. My justification is as follows:
Hope that helps.
Your question alludes to the interesting notion that research in pure math is analogous to investing in stocks (or other financial assets), whereby choosing your research area is akin to choosing which stock to invest in. The idea is that a savvy researcher will cleverly choose the research areas with the highest expected "return on investment" to invest their time in: some research areas are supposedly old and dead, with all the exciting results having been discovered a long time ago so that it is difficult to make any meaningful contributions; while other more recently founded areas are so new and exciting that many "golden" results are metaphorically lying in the streets, just waiting to be picked up by anyone walking by without requiring great talent to uncover. Your question reflects your desire to "pick a winner" and achieve greater success than others who are not so careful to optimize their picks of research area.
Now, how accurate is this analogy? Can one really improve one's odds of success in pure math through such strategizing in the same way that this is possible (though far from easy) to do in the stock market? Well, one school of thought would say that the efficient market hypothesis guarantees that the job market for academic math positions, like the stock market, is efficient, with all the other "players" having already made choices that guarantee that any field one enters is as difficult to produce good work in as any other: new and exciting fields will quickly become so crowded and competitive that one might as well find some less trendy niche research area where you can work by yourself and the lack of competition compensates for the decreased fruitfulness of the subject.
I would argue differently however. I think it's obvious to any experienced mathematician that the "math research market" is not an efficient market (neither is the stock market, incidentally, which is why some investors are consistently successful in making more money than everyone else there) and that it is possible to "pick winners". In fact, the ability to pick winners and invest one's time and effort in fruitful research directions is precisely one of the things that separates successful mathematicians from less successful ones; this ability is part of what we call "talent" (the other part of talent is the talent required to actually solve research problems once you have decided which topic to think about, of course).
After this somewhat abstract discussion, let's get back to your question. I don't think it's unreasonable of you to try to optimize your choice of research area for career success -- as I said, all good mathematicians do this -- but your question does reflect a certain naivete regarding the scale at which this optimization takes place. Each of the areas "number theory", "algebra" and "PDE" that you mention represents such a huge part of mathematics that it is meaningless to ask whether the area is a wise one to do one's research in. This makes no more sense than asking "is it unwise for me to do my PhD in math rather than computer science because math is an old field of research?" As others have said, your actual research topic will be much more specialized than "math" or "computer science" or "number theory" or "algebra". Some research subfields of any of these fields are indeed no longer very productive or trendy, while others are thriving (as a small example, in the "old" area of number theory there has been some incredibly exciting progress recently towards the twin prime conjecture thanks to the work of Yitang Zhang and the follow-up Polymath8 project). The way the optimization actually happens is at a much smaller scale: within very particular research subfields, some researchers are consistently good at asking the right questions, or identifying connections between two seemingly unrelated subfields and making a clever choice to invest their time in thinking hard about both subfields to dig deep into that connection.
Another way in which I see your question as being naive is that you are not taking your natural skills and talents into account. Doing successful research in different areas of math requires hugely different skills. Indeed, I think it's quite rare for anyone to simultaneously consider specializing in either algebra or PDEs, since those are very different areas which require different abilities and tendencies (I find the notion that you are entertaining both simultaneously to be rather amusing). What would be unwise is for you to pick a research area without having any feeling that your particular problem solving skills and other talents are in some way adapted to the area you are picking -- some sense that you are drawn to the field, that you have a good intuitive feeling for it, are good at solving problems in it, and -- ideally -- find it especially interesting, are passionate about it, etc.
To summarize, I think the general idea of considering carefully which research subjects you want to work on in order to maximize your chances of success is a sound one; but it's not really helpful to do this according to broad, simplistic measures of old versus new or trendy versus stale. The best approach is to combine getting advice from multiple experienced people with listening to your own voice regarding which areas you are drawn to and think your talents are suited for, and which problems your intuition tells you are exciting and good research directions to go in. Good luck!
It is not always that you can just "pick an area". The research has to fit with the project that your supervisor has gotten grants for. (S)He can't just ignore what he has promised the financers to research. Given that you are employed by him and tied to a project ( not always the case ), then you better do stuff related to the project or it may look bad for the supervisor for using the money allocated for something to do something else.
No topic is "easy" if you do proper research. Coming up with something new will be hard regardless how popular or trendy is the field you'll be working on.
That being said, you should pick a topic in a field that you find interesting. Suppose you are interested in topology, you should start talking with professors who work in that field. They will tell you what they find interesting and you, after reading some of their work and discussing it with them, could decide whether you'd like to be their student. Once you have an adviser, it's easier to look for a thesis topic in the field of your interest. The adviser will help you pick something that hasn't been done and is a worthy thesis topic.
There is no guarantee that your topic that is fashionable today will still be in fashion in 5 years. As an experienced researcher, you might develop an intuition on where your field of mathematics is going, but, as a student, it's really hard.
What will make you employable as a mathematician, above all, is the quality and quantity of your research output. If you write a few excellent papers during your PhD, it won't matter so much if your field wasn't fashionable. The other thing that might matter for your employability outside academia would be if your thesis topic has direct practical applications. Numerical analysis, statistics, are some fields where you could go.
When trying to decide on topics for a PhD, the advise of older students should be taken with a grain of salt. They aren't necessary experienced researchers, and they don't have the full picture. Talking to postdocs and faculty, attending talks, might help you more. If you are in US, you don't have to make your decision right away, so take your time before you jump.
You are listing areas of work, not topics. You do research within an area, not about an area, so your question title is somewhat misleading. In many ways, your question is analogous to a neuroscience Ph.D. student choosing to do Ph.D. research on "the brain" as opposed to "the spinal cord". To someone in the field you're studying, your question sounds just as naive. People have been doing research on the brain since ancient Egypt, and this will continue for centuries to come.
For all the areas you've mentioned, there are many questions that remain to be answered. In conjuction with your mentors, you will pick a topic within the broad area.
A few thoughts:
Pick a topic you care about. The sort of thing you'd pursue as a hobby because you want to know. You'll need the motivation.
Received wisdom is always worth revisiting, especially as new data and new tools for analysis and simulation come in
What about doing something 'meta' - if so much has been done with these analyses, do methods fall into categories that themselves are worthy of study?
Think about your core idea(s) and do some research into the current state of play, what has been done in the field, and when.
Something/someone that springs to mind is that (Dr.) Brian May of Queen fame was awarded his PhD in 2007 after starting it in 1971. A lot of research can be done in 36 years, but in his case the topic hadn't been explored in the interim.
In the end it is you who will be spending the next 3-4 years on it.
If your motivation is "to get a Ph.D." rather than "to research XYZ" - you should probably not start a Ph.D. program
One of the most common reasons for the stress, depression and feelings of failure that I've encountered as a graduate student union official is people who start a Ph.D. without clear motivations - or with the wrong motivation.
If you're so uncommitted to anything that you're thinking "Oh, I might pick this field, or that field, etc." - then it's not your time to start. And - getting a Ph.D. should not be a goal unto itself, but rather just a byproduct of doing useful research work.
Lot of great answers. But I just want to add one thing that my supervisor told me long ago.
No field is old enough that you cannot do research on it. You just need to dig deeper, ask the right set of questions.
As you know that we do not know everything about anything. So just dump this idea that I should pick a trendy topic. Choose whatever you like (and you can find a supervisor for it), as long as you are asking right questions, every field is worth researching.
Of course number theory and algebra are old areas - both of them date back at least to the Babylonians (hence are at least 3000 years old). Just because something is old it doesn't mean that it is bad. It could also mean that those areas are worthwhile. They were already old 100 years ago. You should look at how number theory was done 100 years ago and how it is done now. Some questions are the similar, but many new ones emerged (for instance in connection with algebraic geometry), and the new ones are as exciting as the old ones.
I think it is wiser for a PhD student to focus on the new ones. This is because the old ones are most likely very hard (if they are interesting, a lot of intelligent people have thought about them and failed). Also, it likely that more people will study the new problems (for the reasons I just mentioned), which means that there are more people for you to talk to (more collaborators) and which might be able to inspire you.
This question does not define its terms (what exactly is "trendy"?, for instance), leading me to suspect it is an unserious query that is close to trolling.
Even so, I'll say that the point of entering a Ph.D. program is to learn how to conduct research and to convey your findings to different audiences, not simply to earn a degree.
If "getting the Ph.D." is your motivation, get out now and do something else that makes you reasonably happy--whether that's coding or running a coffeehouse or needlepoint.
Trust me, there are easier ways to make a living despite the many benefits that accrue to you once you earn the doctorate.
The point of a doctoral dissertation is to conduct a sustained research project that, among the many other arguments that it must make, must demonstrate the significance of its chosen topic(s) and your project's approach(es) to said topic(s).
Otherwise, what's the point? Why go to the trouble?
Finding a topic about which you are passionate and that can meaningfully occupy 2-4 years of your attention is necessary. Trends are just that: trends that ebb and flow. What's "hot" when you begin may be out of fashion by the time you complete the final draft.
You can always survey what's being published and taught in your field(s) of study to determine what's popular at the moment, but a good project makes its own space within its field(s) and subfield(s), so chasing after trends may simply lead to misery rather than enlightenment (or even entertainment).
No, because whatever you do is based on your interest. While doing PhD on the subject you are interested in you need to think before that whether you have passion towards it or not. Unless you show some passion towards your theises or the field you select to move on Even the latest researches are also useless.
My best suggestion to you is that dont ask someone while declaring your research field since you are some passion towards your field you need to think only one thing that how to develop your research in your field. Now go on thinking with a small paper in your hand and let your heart talk to your brain.
And have a good look over all the fields that you are loving and choose something as the best one.
Unless you decide on your own about something you cant succed Since when you start hating it you will blame someone but if you select it on your own YOU CAN EVEN MAKE GOLD OUT OF COAL..
