Planning a PhD project in mathematics
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!