What are examples of (collections of) papers which "close" a field? There is sometimes talk of fields of mathematics being "closed", "ended", or "completed" by a paper or collection of papers. It seems as though this could happen in two ways:


*

*A total characterisation, where somehow "all of the information" about a field has been uncovered.

*A negative result, rendering the field somehow irrelevant.


A possible example for 1 might be the classification of finite simple groups. Examples for 2 might be Goedel's theorem effectively halting Hilbert's programme, or results showing e.g. certain large cardinal axioms to be inconsistent undermining work which assumes it.
What are some other examples of results "closing" a field? 
Are there examples of a small number of papers "completing" a field in the sense of 1 above?
(Apologies for many scare quotes!)
 A: This is possibly a bit of a stretch (in relation to point 2); in that it concerns a modelling assumption which led to a variety of mathematical models which attempted to explain Marconi's transmission of radio waves across the Atlantic in 1901. The assumption was that the radio waves could propagate large distances beyond the horizon primarily via diffraction from the surface of the earth/ocean. The most well-known supporters of this idea (to mathoverflow users ... I assume), in the early twentieth century, were Poincaré and Sommerfeld, who amongst others, studied a variety of boundary value problems with this assumption playing a central role.
The paper that effectively closed this line of mathematical inquiry (almost 20 years old), was written by Watson (at the request of van der Pol) https://doi.org/10.1098/rspa.1918.0050. It is probably fair to say that experimental evidence also contributed to the demise of this idea (see Austin-Cohen reference in the paper ... and amateur experimental evidence) and an earlier paper by Nicholson which is referred to in Watson's paper.
The wider effects of this topic are discussed in detail Yeang's book (see review in the following link).
http://www.reeve.com/Documents/Book%20Reviews/Reeve_BookReview_ProbingSkyRadioWaves_Yeang.pdf
A: Let me preface this by saying that this is just my own account, based on various conversations I've had over the years with many mathematicians, of the following example.
In 1976, William Thurston proved that a closed smooth manifold has a codimension one foliation if and only if it has zero Euler characteristic.  Moreover, every codimension one distribution in the tangent bundle is homotopic to an integrable one.  
While history is always more complicated, at least at the folklore level, this result is said to have caused a mass exodus of people working in the theory of foliations.  You can read about Thurston's point of view on this, which reflects the history being more complicated, in his note Proof and Progress in Mathematics.
Of course, it's absurd to conclude that this "closed" the theory of foliations.  Rather, what I've understood to be the case is that he proved a theorem which was largely expected to be false, and this rendered a nascent industry of building an obstruction theory for co-dimension one foliations largely irrelevant.  Nonetheless, I've been told by many people who know way more about this story than I do that graduate students were actively encouraged to avoid the theory of foliations around this time; the general impression being that Thurston was cleaning up the subject.
A: Index theorem of Atiyah and Singer closed a substantial field of research in the 1960s. I knew people who were working in this field, and had to switch the field of their research
completely.
A more modern example is Louis de Branges proof of the 
Bieberbach conjecture. There was a large field of research, I would say a central field
in analytic functions theory, which could be called "coefficients estimates".
To be sure, it still exists, but nowadays it is considered marginal. Contrary to all expectations, the highly original proof of de Branges's theorem did not lead to a significant further development (so far).
Another commonly mentioned example is Hilbert's results in the 
theory of invariants. They closed the field in some sense, though not forever.
Darij Grinberg's description of this situation as "put to sleep" in his comment brings another similar example to my mind: in 1919/20 Pierre Fatou essentially "put to sleep" the wonderful field of holomorphic dynamics.
He just did everything possible with the tools that existed at that time.
The field was essentially sleeping until the early 1980s, when new, radically new tools were employed and some long standing problems were solved. (There is one isolated exception in this picture: Siegel's theorem of 1942, which also required a new tool, that is called KAM theory nowadays).
It also happens sometimes that a new breakthrough does not really close the field, but many people have to switch to another field because they are not equipped to understand the breakthrough. I do not want to give modern examples of such a sad situation, but according to Lev Pontryagin's own published recollections, he switched from topology 
to applied analysis in 1950s
because the new abstract language introduced by the French revolutionized the area, and he could not stay in line with the modern development. (Pontryagin was one of the most prominent topologists of his time, and he was 42 years old in 1950.)
Another related phenomenon is an appearance of a definitive exposition of a subject which condemns much of the previous work to oblivion. An example
is the book Orthogonal polynomials by Gabor Szego. It did not close the subject,
far from it, but most people stopped reading and citing previous work.
(Same thing that Euclid and Ptolemy did to their predecessors).
A: This is not, perhaps, a very large area, nor a complete "ending", but it was an interesting development in early semigroup theory that I think bears writing down.
Some background, first. A semigroup $S$ is a set with an associative binary operation $\cdot : S \times S \to S$. A semigroup is left cancellative if for all $a, b, c \in S$, we have $ab = ac$ implies $b = c$, and right cancellative if $ba = ca$ implies $b = c$. A semigroup is cancellative if it is left and right cancellative.
All groups are cancellative semigroups, but there are cancellative semigroups which are not groups (free semigroups, for example). Hence being cancellative is a necessary condition for a semigroup to embed in some group. A natural question is the following: does every cancellative semigroup embed in a group?
Anton Sushkevich initiated the study of cancellative semigroups in 1928. He was very interested in the problem of embedding cancellative semigroups in groups, and predicted that this very problem would become a central part of semigroup theory and produce a vast amount of new results in the area. This problem led to several publications by him and several others over the next few years, developing the theory of embedding cancellative semigroups in groups.
In [A. Sushkevich, "Про поширення півгрупи до цілої группы", Zapiski Khark. Mat. 4:12 (1935)], Sushkevich claimed a full affirmative answer -- being cancellative, he claimed, is sufficient for a semigroup to embed in a group!
But alas, in 1937, Malcev proved by way of example that there exists a cancellative semigroup which does not embed inside a group! In fact, he even provided a countable list of necessary and sufficient conditions for a cancellative semigroup to embed in a group, and showed that no finite sublist of this list is sufficient [A. Malcev, "On the Immersion of an Algebraic Ring into a Field," Math Annalen, Bd. 113, 5 Heft (1937)].
And yet, Sushkevich published a book in 1937, "The Theory of Generalised Groups" (of which very few physical copies still remain due to most copies being stored in Kharkov, Ukraine, during WW2, a city which was ruined in numerous battles during the war), which claimed to fix the errors in his original proof. The proof is tricky to read -- and while Sushkevich does acknowledge Malcev's example, he more or less only says "and so a sufficient condition for a semigroup to embed in a group is that it is cancellative and that it is not Malcev's example. 
Malcev turned out to be right, and Sushkevich's proof was wrong (the operation for the "group" he claims to embed the semigroup in is not associative!). Indeed, Sushkevich spent the next few years attempting to remove any trace of his original publication, to the point where I would be surprised if any copy of the paper could be found. So a single counterexample was enough to -- if not "close" -- at least "deflate" the hype around cancellative semigroups.
Of course, as with any result, it only really served to spur further refinements and new lists of sufficient and necessary conditions, but its predicted central importance to semigroup theory fell short, and semigroup theorists mostly moved on to new pastures.
A: Bell's inequality killed the search for the elusive hidden variable theory that was supposed to complete Quantum Mechanics. IMO this qualifies because the result is mathematical.
A: Hilbert's famous work seemed to have killed Invariant Theory. At least that's what Gordan felt at that time. In the historical book by Dieudonn'e' and Carrell  they say  invariant theory, presumed  dead, as coming back alive from the ashes like phoenix.
A: Did Bertrand Russell not close down Frege's programme of logic with his observation of Russell's paradox?  In this case, a simple observation essentially shut down Frege's programme of research, though he did carry on working on it and hoping that the ultimate aim of his project might still be possible in some sense.
A: I get the impression that Freedman's results from the 1980s "closed" the field of topological 4 manifolds, maybe in part because they were perceived as very difficult/intricate (see e.g. questions on MO like this one), but also for the reason 1 of the question asker (they "completely resolved" questions about these manifolds).
A: I don't know a particular paper to which to point, but, from a harmonic analyst's point of view, it seems to me that Weyl's results on compact Lie groups essentially closed the field of "representation theory of compact Lie groups."  (I post this with great trepidation, because this or any answer seems an invitation to someone else to point out in what senses the field proposed is still alive and thriving—but that would be a fun thing to know, too!)
A: In this classic article, Steinitz closed not just one, but all fields. 
A: Alfred Tarski essentially 'closed' the ancient field of Euclidean geometry. Specifically, he provided a simple first-order axiomatisation of Euclidean geometry (where a model is a set of points endowed with a ternary 'betweenness' relation and a quaternary 'congruence' relation, obeying a particular set of axioms) and demonstrated that it is decidable: there exists an algorithm which can take any proposition expressed in the language of Tarski geometry and determine whether it is true or false.
