Should one understand a proof of every important theorem in a field of mathematics to research? I guess not.
However, I think I have to understand proofs of some of them, if not all of them.
So what is the criterion, if any?
What kind of theorem whose proof I can get away with?
EDIT
For example, let me take the main theorems of class field theory.
It's rather easy to understand what they say, but it's difficult to understand the proofs.
Do I have to understand those proofs to research on algebraic number theory?
EDIT
Another example: Hironaka's theorem on resolution of singularities of an algebraic variety in characteristic 0.
I guess most algebraic geometers can do their research without understanding its proof.
EDIT
I'll add more examples.


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*The theorem that singular homology groups satisfy the Eilenberg-Steenrod axioms.

*Most of the basic theorems of homological algebra, for example, the theorem that a filtered complex has a spectral sequence.

*The Feit-Thompson theorem that every finite group of odd order is solvable.

*The classification of finite simple groups(CFSG).
EDIT
I believe this question is becoming more and more important because mathematic is developing faster and faster than before. I guess you are going to give up understaning the proofs of all the important theorems in your field, regardless whether you want to understand them or not.
EDIT
The existence of the field of real numbers.
I'm almost certain that one doesn't need to know its proof to do analysis.
All one needs to know are its properties.
 A: Learn as many as you can, and understand essentially what is driving the proofs.  The ideas show up again and again and again and again and....  You'll start to see patterns, and you'll see new problems that will remind you of old problems that you've seen before.
A: I think it is easier to deal with your examples than with the general question.
Class field theory:  When I teach class field theory, I teach the statements of the results, initially in classical language and then in idelic language.  I spend a lot of time discussing examples, special cases, and applications, such as to classical reciprocity laws, the Kronecker--Weber theorem, and CM of elliptic curves.  My goal is to explain what a class field is, what an abelian extension is, why a priori they are very different concepts, but that they ultimately turn out to be the same.
In terms of proofs, I explain some arguments, especially those that show how group cohomology can be made to interact with statements from classical algebraic number theory (such as Dirichlet's unit theorem) to get a surprising amount of leverage.  (The kind of topics I have in mind are what are classicaly known as genus theory, which lead to the proof of one of the two main inequalities of class field theory.)    The most recent time I taught it, I also sketched the proofs of the basic facts about $L$-functions, following Tate's thesis, and used them to prove the other inequality.  
My goal in selecting topics (apart from time limitations) is to illustrate important ideas, focussing on those which recur throughout the theory.
For a self-studier, some of the background I am discussing can be found in Franz Lemmermeyer's on-line book; other parts are in Cox's book.  Some of them are hard to find in the standard text-book literature.  
If you are reasonably comforable with group cohomology, then you should read the chapter by Washington in Cornell--Silverman--Stevens.  The duality and Euler characteristic theorems that he states there (largely due to Tate) are (non-trivial) consequences of class field theory, but assuming them, you can rederive most of class field theory.  Being able to actually carry out this exercise is a reasonable measure of mastery of the algebraic aspects of class field theory, and is probably more valuable than learning all the technicalities in the proof of class field theory itself.
Resolution: At one point, in terms of the combined measures of importance of its statement, and (at least reputed) difficulty of its proof, Hironoka's theorem was an extreme point in algebraic geometry.  I remember that when I was a graduate student in the mid 90s, there was one particular faculty member who was legendary for his technical abilities, and one of the rumours about him was that he had actually read Hironaka's proof.  
This changed a lot after de Jong proved his theorem on alterations.  De Jong's argument was much more accessible, and more self-evidently geometric, than Hironaka's, and (or at least this was my impression) it led to a new burst of work on all kinds of questions related to resolution of singularities, semistable degeneration, and factorization of birational maps.  Hironaka's proof was revisited, and reworked in a much more accessible fashion. 
There is now a wonderful book of Kollar explaining resolution, and it is very geometric and very accessible.  I certainly don't require my students to read it, but I've recommended it to those of them who are more geometrically inclined.  
The point is that the nature of the proof of resolution, and the way it fits into the rest of algebraic geometry, changed a lot over the last fifteen or so years.  With Kollar's book available, one can learn the ideas of resolution as part of a general education in algebraic geometry, and this greatly enhances the value of learning the proof.  
One realization (due to Grothendieck, I think) is that resolution could be used as a black-box to prove other things (such as his result on equality of algebraic and analytic de Rham cohomology for all smooth varieties).  This kind of application reaches its peak in Deligne's mixed Hodge theory.  When I was a student, and Hironaka's argument itself remained shrouded in mystery for most of us, this was the manner by which we came to grips with resolution, and its geometric significance.  It remains one of the fundamental applictions, and now that we have new insight into resolution and its proof in general, there is hope that we might be able to extend this sort of application to other contexts.  
General conclusions:  Probably there aren't any specific conclusions.  A general lesson that I take away from my own experience of learning math myself, and teaching students, is that it is good to focus on learning arguments, techniques and examples that have significance beyond their immediate context.  As you come to work on a specific piece of research, your focus will also have to become correspondingly more specific, but until you know exactly what specific direction you should focus on, I think the sentiments of the previous sentence are fairly sound advice.  (See also my advice on learning arithmetic geometry in this thread.)
Added in response to OP's edit: The later examples that you give are of greatly divergent difficulty.  The basic theorems of homological algebra are essentially exercises (there is a well-known remark by Lang to this effect), and easily learnt.   The proof that singular homology satisfies the Eilenberg--Steenrod axioms is also fairly straightforward (or at least the key idea --- simplicial approximation --- is easily grasped).  Treating singular homology and homological algebra as black-boxes is more or less unnecessary, and since the proofs are closely aligned with the basic statements of the theory, I think it would also be a mistake.  
The results in group theory that you mention are of a different nature.  They also come up less often, but when they do, they are often treated as black-boxes.  People are also known, though, to go to efforts to avoid appealing to the classification of finite simple of groups, because of its black-box nature, and because of lingering questions about the reliability of what's inside the box.
