Planning a PhD project in mathematics I am obliged to hand in an an exposé outlining my PhD project in mathematics, including some kind of working plan. Since it is answered here and since it can be easily found on the internet, I have some understanding about what such a working plan should look like.
However, when it comes to fleshing this out, I have large difficulties. But I am sure that I am not the first would-be mathematician writing a working plan in the world, so how do others do it?
What I struggle with. For instance, I have no idea of what I want to achieve within the (expected) three years of my studies, and apparently, since we fixed a very broad working title for my thesis, neither has my supervisor.  My Master's was in a different field with only minor connections to the one I am about to start my PhD in.
Therefore, I expect that I spend the first weeks or months getting used to the field, reading literature, working on small problems of which hopefully one turns out to be interesting and fruitful enough to build a theses on.
But I have no idea how to foresee when I will be done with spending most of my time on literature, when I will have solved which problem and finished the proof for what theorem, when I will start compiling my results into a thesis, when to write which chapter of it or when I will hand in a paper with what title to which journal.
How I've solved the problem in the past. To my shame, I have to admit that when writing my Master's thesis, I had not made any plan either. I just worked into the day and in the end, there was a thesis. I am aware that this is a very inefficient working style, but apparently, expectations towards my thesis were low enough such that it worked out. I expect that for a PhD, working in such an unstructured fashion does not work out any more; therefore, I am actually motivated to give my work more structure.
If you don’t have at least one research problem, you can’t write a plan.
That’s the core of your difficulty (based on your comment in which you explained that you don’t have a research problem). A plan is the articulation of what your objectives are and how you think you might achieve them. But you don’t actually have any concrete objectives. So the idea of writing a plan is unattainable - you’re not even in a position to get started doing this. It is a classic case of putting the cart before the horse.
Now, let’s talk about what a research problem actually is in pure mathematics. You mention proving a conjecture, that’s certainly a type of research problem and the most concrete and well-defined one. If someone asks you to come up with a research problem, stating that you want to prove someone’s conjecture is the easiest type of problem to come up with, but on the other hand it’s probably the hardest to actually solve since presumably other people are also trying and have not yet succeeded. So for a PhD project it’s perfectly acceptable (and usually advisable) to be a bit less ambitious and have slightly less concrete goals. Such goals can be along the lines of:

Improve a known result from the literature, by weakening the hypotheses and/or strengthening the conclusion.
(E.g., if Jones proved that all infinitely differentiable frombloids are magnabulous and you manage to prove that it’s enough to assume only seven times differentiability, you’ve improved on Jones’ result.)

Prove an analogue of a known result
(E.g., “all p-adic frombloids are semi-magnabulous in the Smith topology”, when you are the first to study p-adic frombloids but are guided by Jones’s ideas in the differentiable case.)

Prove a variant of a known result with stronger hypotheses and stronger conclusions, or weaker hypotheses and weaker conclusions, or hypotheses that are neither strictly stronger nor strictly weaker than the original.

Sharpen a numerical constant in a known result
(E.g., “the fractal dimension of a magnabulous frombloid is bounded by 17.781”, when Jones proved the bound 27.13)

Prove (or disprove) a converse to a known result

Etc etc.


Now, the point here is that research problems exist on a spectrum of vagueness-concreteness. It’s okay to not have a completely accurate idea of what it is that you want to prove when you get started (as someone said, that’s what makes it research). Very experienced researchers even sometimes start thinking about a research area with a completely vague goal of the type “I want to understand [research area/class of objects/etc] better” (I know that I sometimes do this myself). But there’s a strong caveat here: you are a PhD student. A goal that is suitable for an experienced (not to mention tenured) researcher is not necessarily suitable as one that a PhD student should be given to try and solve with the expectation that there will be a reasonably high likelihood of success. And specifically, for a PhD student I think it’s pretty essential that the goal should be fairly concrete. Just “I want to understand X better” is not a recipe for success at your stage, and in fact even for experienced researchers it often leads nowhere.
So what should you do? Talk to your advisor. Explain to them that you think the project should be fleshed out some more before you begin writing your exposé and that you need some actual, specific problems. It is their responsibility to help you find problems that are suitable to work on; ideally you should have not just one but at least three or four fairly concrete goals, of a more or less realistic level of difficulty for your level of training when you start out. If your advisor isn’t able to help you come up with some ideas like that and bring you to a point where you can start putting a plan on paper, sadly they are probably not a very good advisor, and you might have more serious things to worry about for the future of your project than just the current difficulties with writing the plan. Anyway, hope this helps and good luck!