New proofs to major theorems leading to new insights and results? I am wondering, historically, when has a new proof of an old theorem been particularly fruitful. A few examples I have in mind (all number theoretic) are:
First example is classical... which is Euler's proof of Euclid's theorem which asserts that there exist infinitely many primes. Here is when the factorization $\displaystyle \prod_p (1-p^{-s})^{-1} = \sum_{n=1}^\infty \frac{1}{n^s}$ was first introduced, leading of course to what is now known as the Riemann Hypothesis.
Second example is when Hardy and Littlewood gave an alternative proof of Waring's problem, which was done by Hilbert earlier. Their proof introduced what is now known as the Hardy-Littlewood Circle Method and gave an exact asymptotic for the Waring bases, which is stronger than Hilbert's result which only asserted that every sufficiently large positive integer can be written as the sum of a bounded number of $k$th powers. Later on the Hardy-Littlewood method proved very fruitful in other results, namely Vinogradov's Theorem asserting that every sufficiently large odd positive integer can be written as the sum of three primes.
Third example is Tim Gowers' alternate proof to Szemerédi's Theorem asserting that every subset of the positive integers with positive upper density contains arbitrarily long arithmetic progressions. This advance, namely the introduction of Gowers uniformity norms, led eventually to the Green-Tao Theorem proving the existence of arbitrarily long arithmetic progressions in the primes. 
So I am wondering if there exist other incidences (number theory related or not) where a new proof really gave legitimate new insights, perhaps even a proof of a (major) new result.
Edit: I am primarily interested in examples where a new proof sparked off a new direction in research. This is best supported by having a major new theorem proved using techniques inspired by the new proof. An example of something that I am not interested in is something like Donald Newman's proof of the prime number theorem, which while elegant and 'natural' as he puts it, has seen limited generalization to other areas and one is hard pressed to apply the same technique to other problems. 
 A: The Manin-Mumford Conjecture, first proved by Raynaud in 1983, states that the points on a curve $X$ of genus 2 or more that are torsion when embedded into its Jacobian are finite in number. The bound is also independent of how you embed the curve (that is, it is independent of the "base point"). 
Ken Ribet reproved this using the notion of an "almost rational torsion point". This is cool because it can lead to explicit versions of Manin-Mumford. The idea is that the set we're interested in is contained in the set of almost rational torsion points, which Ribet proves is finite, together with hyperelliptic branch points if the curve happens to be hyperelliptic. 
So finding the almost rational torsion on jacobians of curves might help make things explicit. Doing this for modular jacobians, Ribet proved that
$X_0(N) \cap J_0(N)_{tors} = \{0,\infty\}$, 
unless $X_0(N)$ is hyperelliptic, in which case you simply add the branch points. 
To be honest I should say that this theorem was first proved by Matthew Baker (who actually gives two proofs), and independently around the same time by A. Tamagawa. Ribet's approach is similar to Bakers' second approach. For a survey, google "Torsion points on modular curves and Galois theory" to summon a pdf by Ribet and Minhyong Kim.
A: Hrushovski's Model-Theoretic proof for the Mordell-Lang conjecture over function fields is an example.  
A: Here are a few examples from the 19th century.


*

*Unsolvability of the quintic equation. Abel (1826) proved this by algebraic
ingenuity, but without clarifying the concepts involved. Galois (1830) gave a
proof that introduced the concepts of group, normal subgroup, and solvability
(of groups), thus laying the foundations of group theory and Galois theory.

*Double periodicity of elliptic functions. Abel and Jacobi established this
(1820s) mainly by computation. Riemann (1850s) put elliptic functions on
a clear conceptual basis by showing that the underlying elliptic curve is a
torus, and that the periods correspond to independent loops on the torus.

*Riemann-Roch theorem. Riemann (1857) discovered this theorem using
Riemann surfaces, but applying physical intuition (the "Dirichlet principle").
This principle was not made rigorous until 1901. In the meantime, Dedekind
and Weber (1882) gave the first rigorous and complete proof of Riemann-Roch,
by reconstructing the theory of Riemann surfaces algebraically. In the process
they paved the way for modern algebraic geometry.
A: Hilbert basis theorem, a nonconstructive proof replacing and generalizing a monstrous explicit calculation ("this is not mathematics, this is theology").
A: If you're interested in something that's expected to do this (here, with a related paper here), but is a very current project, there's Lazic's proof of the finite generation of (log) canonical rings.  I don't know of any great insights gained from the new proof, other than the surprising fact that it's POSSIBLE to prove it this way, and that the method, rather than requiring the Mori program to prove the theorem, allows a proof of many important theorems in the Mori program from it.  This is, though, quite a work in progress.
A: Serre's construction of the $p$-adic zeta function, using the fact that the values of the Riemann zeta function at negative integers are constant terms of Eisenstein series.  This paved the way for a lot a mathematics including the proof of Iwasawa main conjecture by Mazur and Wiles. 
A: Tamarkin's proof of Kontsevich's formality theorem. It greatly deepened and expanded the whole subject of deformation quantization. One of the first and most successful applications of the theory of deformations of operad morphisms.
A: A very nice example in my eyes is Serre's proof of Riemann-Roch:

Sometimes, you are just not satisfied with existing proofs, and you look for better ones, which can be applied in different situations. A typical example for me was when I worked on the Riemann-Roch theorem (circa 1953), which I viewed as an "Euler-Poincare" formula (I did not know then that Kodaira-Spencer had had the same idea.) My first objective was to prove it for algebraic curves - a case which was known for about a century! But I wanted a proof in a special style; and when I managed to find it, I remember it did not take me more than a minute or two to go from there to the 2-dimensional case (which had just been done by Kodaira). 

He is speaking, of course, of the sheaf-theoretic proofs, which are usually presented today. This was the period where he was working on FAC, GAGA and his duality theorem, which revolutionized algebraic geometry. 
A: The classic example from mathematical physics is Richard Feynman's Space-Time approach to nonrelativistic quantum mechanics (1948), which (in essence) proved that the Green function of the Schroedinger equation was equal to a path integral. The article begins:

It is a curious historical fact that modern quantum mechanics began with two quite different mathematical formulations: the differential equation of Schroedinger, and the matrix algebra of Heisenbert.  [...] This paper will describe what is essentially a third formulation of non-relativistic quantum theory.

As for the value of seeking multiple derivations, we have Feynman's Nobel Address The Development of the Space-Time View of Quantum Electrodynamics (1965):

There is always another way to say the same thing that doesn't look at all like the way you said it before. I don't know what the reason for this is. I think it is somehow a representation of the simplicity of nature. [...] Perhaps a thing is simple if you can describe it fully in several different ways without immediately knowing that you are describing the same thing.

In a classical context, we have Saunders Mac Lane in Hamiltonian mechanics and geometry (1970)  presenting new geometric analyses of old dynamical problems:

Mathematical ideas do not live fully till they are presented clearly, and we never quite achieve that ultimate clarity. Just as each generation of historians must analyse the past again, so in the exact sciences we must in each period take up the renewed struggle to present as clearly as we can the underlying ideas of mathematics. 

In the mid-1970s these various derivations came together as Fadeev and Popov's (1974) Covariant quantization of the gravitational field, which provided the foundations for todays' gold-standard method of BRST quantization, for which van Holten's Aspects of BRST quantization (2002) is a good review:

Quite often the preferred dynamical equations of a physical system are not formulated directly in terms of observable degrees of freedom, but in terms of more primitive quantities [...] Out of these roots has grown an elegant and powerful framework for dealing with quite general classes of constrained systems using ideas borrowed from algebraic geometry.

By this 90-year process of successive rederivations, we nowadays have arrived at a more nearly global appreciation—encompassing both classical and quantum dynamics—of the ideas that Terry Tao's essay What is a Gauge? discusses.
Cutting-edge research in classical, quantum, and (increasingly common) hybrid dynamical systems uses all of these mathematical approaches, each formally equivalent to all the others ... but with very different ideas behind them.  The resulting naturality has lent new passion to the longstanding romance between mathematics and physics.
A: Witten's supersymmetric proof of the Atiyah-Singer index theorem.
A: S.S.Chern's intrinsic proof of Gauss–Bonnet theorem.
