Is it a contribution if I prove the result in previous paper in my own way and provide small extension in the form of application of the results? If I have an idea to extend an already published paper (P1) but the extension is very small and further I know how to prove the results of (P1) so my question is as follows. If I prove the results of P1 through my own way and has slight extension (in the form of application of the results) of P1 then is it worth writing that idea or should I avoid such thing?
It is often very difficult to answer "Is this paper worth writing?" in general terms.  Sorry to say, but it is very common that you don't know whether a paper is worth writing until you write it, and you don't know whether a paper is publishable until you submit it (sometimes more than once).  

If I understood the situation properly, it's this: there is a paper in the literature by someone else that contains some mathematical-ish result: something that received a proof in the original publication.  You have (i) your own proof and (ii) a small extension of the result, and you are wondering whether it's worth writing up and trying to publish.  So the answer is: it might or might not be.  If you are a junior researcher -- by which I mean anyone who has a designated advisor or mentor -- then I strongly suggest that you talk to your advisor about this.  The question of what constitutes publishable work (and if so, where it can/should be published) is really a question about the sociology of your discipline, and a veteran researcher in your field will probably have better instincts about this than a newer researcher...and this can continue to be true even when the veteran researcher has equal or lesser insight into this particular project.  

Probably though at some point you will just have to decide whether to push on with it or not.  That's really up to you.  The main downside is that you may spend time writing and trying to publish the paper and eventually learn that the paper is not publishable, or at least not publishable in the sort of journal you want to publish in.  There is also the chance that you could publish the paper and that others in the field may view your contribution as too minor to meet their own standards of publication, but in that situation I would expect them to mostly ignore the paper.  (There are other situations in academia where people count papers, and even a very minor publication will still count for that.  This is not a great situation, in my opinion, but it exists, and some people may in fact have large incentives to keep the publications coming.)  

I think the right way to look at the decision is this: the question is not really whether to write up and publish versus not to write up and publish.  Rather, you will want to spend your time writing up and publishing something, and practically speaking there is a limit on the number of projects you can try to write up and publish at any given time.  (This varies based on the field and even the person.  For me (a mathematician), even if I start with a huge stack of manuscripts already on my desk with all the Theorem:... and Proof:...'s already written down in some mathematically satisfactory form, nevertheless I would struggle mightily to find the time to edit and submit more than 4-5 of them per year.)  So do you want to spend your time on this or something else?

I want to end by mentioning that a few months ago I submitted for publication a project that has the same rough description as the OP: in this note I give a new (though not completely new) proof of a recent theorem of M. Kapovich, and then I prove a stronger result in a special case.  There is no question that I view this as a very minor work.  Why did I decide to submit it for publication?  Well, first I found Kapovich's result very interesting so I had already decided to give an exposition of it in some notes of mine.  Writing up these results led directly to my (very minor) new contribution, so the amount of additional polishing I had to do in order to have something submittable was rather small.  Second, the paper concerns a mathematical subfield, complex manifolds, in which I absolutely do not possess a research-level knowledge....so I have no reputation to ruin.  Finally, I have enough other publications that I think no one is going to try to draw any conclusions about my research program or trajectory from this one paper.  Whether this was a good decision is not yet clear to me...

Added: Just this morning I received an email that the above note has been accepted!