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In the empirical sciences, there are a number of journals that publish 'negative' results. Negative or null results occur when researchers are unable to confirm the findings obtained from earlier published reports. In the applied sciences, they may also come about when a scientist aims to to show that a particular technology (e.g., CRISPR) could alleviate a problem (e.g., a particular virus that kills that kills a specific type of plant), only to find out that it does quite the opposite (e.g. the technology led to the evolution of viruses that were more resistant to CRISPR).

In the formal sciences, including mathematics and logic, experiments like these aren't conducted*. However, it does happen that mathematicians develop machinery to tackle a particular thorny problem, only to find out it doesn't work. A good example is John R. Stallings' false proof of the Poincaré Conjecture.

Publications like these are few and far between. It seems to me that one of the reasons this is the case, is that there aren't any journals that are specifically geared to these types of papers. They are predominantly focussed on publishing articles that obtain 'positive' results, i.e. actually prove theorems or refute conjectures.

Yet it also appears to me that papers like these can be very useful to researchers in mathematics, for the following reasons:

A. They may inspire someone to slightly tweak the failed approach, in order to make it work and actually prove the theorem(s);

B. They may allow someone to see what has already been tried, and what types of avenues of research are probably not worth pursuing;

C. They may provide a platform for approaches to tackling difficult problems in mathematics, even if the methods don't work so far. Thus, they provide a place to share ideas, rather than throwing away months of work.

My question is twofold:

  1. Are there already any journals that are devoted to papers containing negative results in the above sense?
  2. Would it be worthwhile to set up such a journal, from your perspective?

(*) I am aware that experimental mathematics is a thing. The focal point of this question isn't really the experimental nature of the mathematics research, but it's about offering a venue to the failed approaches to solving problems developed through research - formal, experimental or otherwise.

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    $\begingroup$ "In the formal sciences, including mathematics and logic, experiments like these aren't conducted." - this isn't strictly speaking true, experimental mathematics is a thing, and there are journals dedicated to it. I vaguely recall seeing some papers in them which were of more "negative" nature too. This doesn't address the main points of your question though so I will keep it to a comment $\endgroup$
    – Wojowu
    Oct 23 at 15:32
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    $\begingroup$ I think one issue with your implicit proposal, as basically suggested by YCor, is that this is simply not how math journals are organized. It's like asking if there is a journal dedicated to proofs by contradiction. A failed (but interesting!) attempt to e.g. prove the Poincaré conjecture might be published in a journal dedicated to geometry/topology; a failed attempt to prove the Riemann hypothesis might be published in a number theory or an analysis journal. $\endgroup$ Oct 23 at 16:26
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    $\begingroup$ @SamHopkins, you say "might be published"; but are they? Without saying that they don't exist, I can't think of any papers in my field that are intentionally of the shape "we tried this proof technique, and it doesn't work." There are definitely papers found in retrospect to have errors, or papers describing only partially successful solutions, but I can't think of any of the form "this might seem like a good proof technique, but actually it isn't." $\endgroup$
    – LSpice
    Oct 23 at 16:28
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    $\begingroup$ To me, this idea sounds like it has potential. More than anything, I imagine that the composition of its editorial board would determine whether such a journal would succeed and be valuable. With some respected, responsible, and discerning mathematicians from a variety of fields on the editorial board, authors would likely be intrigued by the experiment, and ready to send some interesting and worthwhile papers to such a journal. Then I think you have the beginning of a successful journal. $\endgroup$
    – A.S.
    Oct 23 at 16:31
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    $\begingroup$ @LSpice: I think it might just be a matter of how papers are phrased. For example, suppose there are two important objects $X$ and $Y$ in some subfield, and there is a question of whether perhaps $X=Y$. A paper might compute some invariant of both $X$ and $Y$ and observe they are the same. This could be (but is usually not) thought of as a failed attempt to prove that $X\neq Y$. $\endgroup$ Oct 23 at 16:34
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I don't really know what an answer is for a question like "what about ...?" but I have some thoughts.

In fact, way back around 2006-2007 (according to the dates on the ArXiv, see Multiplying Modular Forms, if you want). What happened was I had written what I thought was a really nice paper explaining how to multiply modular forms whose associated representations (of a real Lie group) belonged to the discrete series. It clarified (to me) some ideas of others, and seemed to extend to all sorts of other kinds of modular forms like those on the exceptional group $G_2$.

Well... I was all happy about this and about to speak at a conference. But the day before, Gordan Savin told me about a mistake in the paper. I spent a long evening kicking around the paper and then kicking myself about it. It was a really subtle thing to me -- a difference between $K$-fixed vectors and $K \times K$-fixed vectors -- but a "well-known" issue to experts, ultimately involving the failure of discrete decomposability.

Anyways, the next day at the conference (AMS Special Session, Jan 8, 2007), I didn't really know what to say, but I suggested that someone start the "Journal of Doomed Proofs". And I wasn't kidding. It would be refereed and everything. Criteria for acceptance would be the following:

  1. The paper contains an plausible approach to a problem of interest to the mathematical community.

  2. The approach is sufficiently motivated that many other people might try it.

  3. The approach is doomed, though not obviously from the beginning.

  4. The paper explains why the approach is doomed, identifying the obstacles which really stop things from working. Or at least have to be worked around in the future.

I still think this is a good idea, and not just for the usual "science should publish negative results" reason. Mathematicians have a sort of secret oral tradition of "well-known" things (doomed ideas, silly apocrypha, the largest rank of an elliptic curve over Q, etc.). But those of us who teach in redwood forests don't really have access to this tradition any more. And some were never granted access in the first place. A journal might go a little way to correct this.

If anyone knows how to pitch a new journal, count me in. If it's JDP (Journal of Doomed Proofs) or JNR (Journal of Negative Results) or whatever, it's fine with me. But not with Elsevier please.

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    $\begingroup$ Great story! Nice to see you've been thinking along the same lines. I also completely agree with the criteria for acceptance you've laid out $\endgroup$
    – Max Muller
    Oct 24 at 9:40
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    $\begingroup$ @Marty Did you try publishing your work anyway? Maybe what is needed isn't for the community to set up a journal, but for authors like you to recognize that their work is valuable and make the effort to write it up in a way that makes that value clear. $\endgroup$ Oct 24 at 12:58
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    $\begingroup$ @TimothyChow Yes, in fact the article is published. I recall it getting rejected from a journal at first, because the results were more negative than positive. But then it ended up published by Cambridge Univ. Press in the volume "Modular Forms on Schiermonnikoog", in 2008. $\endgroup$
    – Marty
    Oct 24 at 21:24
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There have been papers like the following in the American Mathematical Monthly

Guy, Richard K., "Unsolved Problems: Don't Try to Solve These Problems". Amer. Math. Monthly 90 (1983), no. 1, 35–38+39–41.

The suggestion being that graduate students and beginning mathematicians would likely waste a lot of time and not get anywhere if they attack these problems.


The original version of this post confused the above Monthly department with another one called "Research Problems", which ran from 1969 to about 1980. The first was on what P.J.Kelly called the "Spoke Problem".

Klee, Victor; Research Problems: "Can a Plane Convex Body have Two Equichordal Points?" Amer. Math. Monthly 76 (1969), no. 1, 54–55.

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    $\begingroup$ This is a blog post and not a proper article, but Terry Tao's "Why global regularity for Navier-Stokes is hard" (terrytao.wordpress.com/2007/03/18/…) has sort of the same flavor of explaining why standard techniques have not worked for a notorious open problem. $\endgroup$ Oct 24 at 12:37
  • $\begingroup$ @SamHopkins Is this the same work that none mentioned? $\endgroup$ Oct 24 at 13:00
  • $\begingroup$ @TimothyChow: Not exactly. none referenced a novel approach to Navier-Stokes that Tao proposed (see, e.g., terrytao.wordpress.com/2014/02/04/… for a blog discussion of that). What I linked to was Tao's discussion of why standard approaches are unlikely to succeed. $\endgroup$ Oct 24 at 13:09
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    $\begingroup$ @GeraldEdgar Do you remember the statement of the "Spoke Problem"? If you can provide a description, maybe someone can help locate the article. $\endgroup$ Oct 25 at 8:00
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    $\begingroup$ @SamHopkins, seven years later Tao went from “why global regularity for Napier-Stokes is hard” to “finite-time blowup for an averaged three-dimensional Navier-Stokes equation”, and that became a published article in the Journal of the AMS. $\endgroup$
    – Matt F.
    Oct 26 at 0:36
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Failed attempts can be documented in technical reports which one can post online if so desired. A technical report is a way to communicate to your superiors, or a funding agency that you put in an effort, which unfortunately led nowhere. Also a technical report could be a note to yourself, a record of what you thought about at a given time.

Of course, failed attempts are common, as most of the things we try as mathematicians fail. I personally find it hard enough to keep up with ever-growing record of successful attempts. In my opinion there are very few people whose failed attempts are worth reading, and hence in most cases publishing failed attempts is a waste of resources. Posting them on one's homepage is certainly okay.

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There was a workshop on "Barriers" in computational complexity a while back. A barrier result is one showing that a certain approach to solving a given problem (such as P vs NP) can't possibly work. I'm having trouble finding info about the workshop but here is an overview of the topic:

http://pi.math.cornell.edu/~takhmejanov/BarriersInComplexity.pdf

It would be interesting to have a collection of such articles from various areas of mathematics. Terence Tao's use of self-replicating fluid "automata" to show you can't prove Navier-Stokes regularity using energy conservation is another example. A whole journal might be hard to fill though.

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  • $\begingroup$ You're right, it's surprisingly hard to find info about the workshop. The Wayback Machine has archived some material from the first Barriers workshop in 2009, but for the second workshop in 2010, all I've been able to find is a list of talks here with a bunch of dead links. $\endgroup$ Oct 24 at 20:01
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(Too long for a comment, but probably more opinionated and mildly off topic than a good answer. My apologies.)

It seems like there are two distinct issues at hand here suggesting why one should want such a journal. The first is where barriers or obstructions are subtle but known folklore in a specific community. The second is when a single person has tried a specific tactic and it doesn't work, and they can identify that it doesn't work for reasons $X$, $Y$, and $Z$. There may sometimes be overlap between these two issues but the first is part of a more general problem, of folklore in general, so I am almost inclined to think that there should be a journal of folklore results, but maybe the Arxiv is better suited for that.

At least or some specific problems, it seems like obstructions are themselves studied or are included in papers addressing related issues. For example, consider the very old open problem of whether there are any odd perfect numbers. Recently, Pace Nielsen and a collection of other researchers published a paper on a generalized version of "spoof odd perfect numbers" which are numbers which would be an odd perfect number if one pretends that a specific factor is prime. The classic example here is due to Descartes who looked at $$N=3^27^211^213^2 22021$$ where at a glance it seems to be an odd perfect number because if we ignore that $22021=19^2 61$, we would have $\sigma(N) = (3^2+3+1)(7^2+7+1)(11^2+11+1)(13^2+13+1)(22021+1) = 2N$. Here, $\sigma(N)$ should be the sum of the divisors of $N$, but we are applying the formula for it as if 22021 were prime. John Voight generalized this idea, allowing one to have negative prime factors in a spoof, and this was further generalized by Nielsen's group who allowed repeated prime factors where one doesn't recognize that the they are the same prime. Now, the interesting bit here is that many of the results proven about odd perfect numbers in the literature have proofs which essentially go through with only small modification to prove analogous statements about this broader class of numbers. This means that those results cannot by themselves hope to prove there are no odd perfect numbers. This is also useful if one is asked to referee papers claiming to prove that there are no odd perfect numbers or claiming very strong results about them. One can go through the entire argument using Descartes number or one of the other examples, and often the error will pop up that way.

In a different direction but also on the same problem, I recently introduced another obstruction in this paper. There, the primary idea was the following: Euler proved that any odd perfect number $N$ must satisfy that $N = q^e m^2$ where $q$ is a prime and $q \equiv e \equiv 1$ (mod 4), and $(q,m)=1$. (This is by modern standards pretty trivial. It isn't even really a statement about an odd perfect number, but a statement about any odd number $n$ where $\sigma(n) \equiv 2$ (mod 4).) It turns out that many of the statements about odd perfect numbers that have been proven are weak in the following sense. Given a set of positive integers $S$, we'll write $S(x)$ to be the number of elements in $S$ which are at most $x$. Write $E(x)$ to be the set of numbers satisfying Euler's restriction. Given a property $p$, we'll write $E_p$ to be the set of elements in $E$ which satisfy property $p$. Then most properties $p$ in the literature which have been proven about odd perfect numbers satisfy $$\lim_{x \rightarrow \infty} \frac{E_p(x)}{E(x)}=1.$$ That is, the property applies to almost all elements in the set $E$. Now, no finite collection of such properties can prove that no odd perfect numbers exist. Again, this is also pretty useful for trying to find holes in claimed proofs of the conjecture if one wants to do that sort of thing.

As far as I can tell, while there are some results which manage to partially evade the spoof obstruction, and some which manage to evade the density issue, there's nothing in the literature which seems to fully evade both.

But all of these are things which have managed to go in existing papers. Are there similar ideas which are not getting put in the literature to a large extent? I'm less certain of that.

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