## Why you shouldn’t be too pessimistic

In our math research we make countless choices. We chose a problem to work on, decide whether its claim is true or false, what tools to use, what earlier papers to study which might prove useful, who to collaborate with, which computer experiments might be helpful, etc. Choices, choices, choices… Most our choices are private. Others are public. This blog is about wrong public choices that I made misjudging some conjectures by being overly pessimistic.

#### The meaning of conjectures

As I have written before, conjectures are crucial to the developments of mathematics and to my own work in particular. The concept itself is difficult, however. While traditionally conjectures are viewed as some sort of “*unproven laws of nature*“, that comparison is widely misleading as many conjectures are descriptive rather than quantitative. To understand this, note the stark contrast with experimental physics, as many mathematical conjectures are not particularly testable yet remain quite interesting. For example, if someone conjectures there are infinitely many *Fermat primes*, the only way to dissuade such person is to actually disprove the claim.

There is also an important social aspect of conjecture making. For a person who poses a conjecture, there is a certain clairvoyance respected by other people in the area. Predictions are never easy, especially of a precise technical nature, so some bravery or self-assuredness is required. Note that social capital is spent every time a conjecture is posed. In fact, a lot of it is lost when it’s refuted, you come out even if it’s proved relatively quickly, and you gain only if the conjecture becomes popular or proved possibly many years later. There is also a “*boy who cried wolf*” aspect for people who make too many conjectures of dubious quality — people will just tune out.

Now, for the person working on a conjecture, there is also a *betting aspect* one cannot ignore. As in, are you sure you are working in the right direction? Perhaps, the conjecture is simply *false *and you are wasting your time… I wrote about this all before in the post linked above, and the life/career implications on the solver are obvious. The success in solving a well known conjecture is often regarded much higher than a comparable result nobody asked about. This may seem unfair, and there is a bit of celebrity culture here. Thinks about it this way — two lead actors can have similar acting skills, but the one who is a star will usually attract a much larger audience…

#### Stories of conjectures

Not unlike what happens to papers and mathematical results, conjectures also have stories worth telling, even if these stories are rarely discussed at length. In fact, these “** conjecture stories**” fall into a few types. This is a little bit similar to the “

*types of scientific papers*” meme, but more detailed. Let me list a few scenarios, from the least to the most mathematically helpful:

**(1)** * Wishful thinking*. Say, you are working on a major open problem. You realize that a famous conjecture

**A**follows from a combination of three conjectures

**B**,

**C**and

**D**whose sole motivation is their applications to

**A**. Some of these smaller conjectures are beyond the existing technology in the area and cannot be checked computationally beyond a few special cases. You then declare that this to be your “

*program*” and prove a small special case of

**C**. Somebody points out that

**D**is trivially false. You shrug, replace it with a weaker

**D’**which suffices for your program but is harder to disprove. Somebody writes a long state of the art paper disproving

**D’**. You shrug again and suggest an even weaker conjecture

**D”**. Everyone else shrugs and moves on.

**(2)** ** Reconfirming long held beliefs**. You are working in a major field of study aiming to prove a famous open problem

**A**. Over the years you proved a number of special cases of

**A**and became one the leaders of the area. You are very optimistic about

**A**discussing it in numerous talks and papers. Suddenly

**A**is disproved in some esoteric situations, undermining the motivation of much of your older and ongoing work. So you propose a weaker conjecture

**A’**as a replacement for

**A**in an effort to salvage both the field and your reputation. This makes happy everyone in the area and they completely ignore the disproof of

**A**from this point on, pretending it’s completely irrelevant. Meanwhile, they replace

**A**with

**A’**in all subsequent papers and beamer talk slides.

**(3)** ** Accidental discovery.** In your ongoing work you stumble at a coincidence. It seem, all objects of a certain kind have some additional property making them “

*nice*“. You are clueless why would that be true, since being

*nice*belongs to another area

**X**. Being

*nice*is also too abstract to be checked easily on a computer. You consult a colleague working in

**X**whether this is obvious/plausible/can be proved and receive No/Yes/Maybe answers to these three questions. You are either unable to prove the property or uninterested in problem, or don’t know much about

**X**. So you mention it in the

*Final Remarks*section of your latest paper in vain hope somebody reads it. For a few years, every time you meet somebody working in

**X**you mention to them your “nice conjecture”, so much that people laugh at you behind your back.

** (4) Strong computational evidence.** You are doing computer experiments related to your work. Suddenly certain numbers appear to have an unexpectedly nice formula or a generating function. You check with OEIS and the sequence is there indeed, but not with the meaning you wanted. You use the “

*scientific method*” to get a few more terms and they indeed support your conjectural formula. Convinced this is not an instance of the “

*strong law of small numbers*“, you state the formula as a conjecture.

**(5) Being contrarian. ** You think deeply about famous conjecture

**A**. Not only your realize that there is no way one can approach

**A**in full generality, but also that it contradicts some intuition you have about the area. However,

**A**was stated by a very influential person

*N*and many people believe in

**A**proving it in a number of small special cases. You want to state a

**non-A**conjecture, but realize the inevitable PR disaster of people directly comparing you to

*N*. So you either state that you don’t believe in

**A**, or that you believe in a conjecture

**B**which is either slightly stronger or slightly weaker than

**non-A**, hoping the history will prove you right.

**(6) Being inspirational.** You think deeply about the area and realize that there is a fundamental principle underlying certain structures in your work. Formalizing this principle requires a great deal of effort and results in a conjecture

**A**. The conjecture leads to a large body of work by many people, even some counterexamples in esoteric situations, leading to various fixes such as

**A’**. But at that point

**A’**is no longer the goal but more of a direction in which people work proving a number of

**A**-related results.

Obviously, there are many other possible stories, while some stories are are a mixture of several of these.

#### Why do I care? Why now?

In the past few years I’ve been collecting references to my papers which solve or make some progress towards my conjectures and open problems, putting links to them on my research page. Turns out, over the years I made a lot of those. Even more surprisingly, there are quite a few papers which address them. Here is a small sampler, in random order:

**(1)** Scott Sheffield proved my *ribbon tilings *conjecture.

**(2)** Alex Lubotzky proved my conjecture on *random generation* of a finite group.

**(3)** Our generalized *loop-erased random walk* conjecture (joint with Igor Gorodezky) was recently proved by Heng Guo and Mark Jerrum.

**(4)** Our *Young tableau bijections* conjecture (joint with Ernesto Vallejo) was resolved by André Henriques and Joel Kamnitzer.

**(5)** My *size Ramsey numbers* conjecture led to a series of papers, and was completely resolved only recently by Nemanja Draganić, Michael Krivelevich and Rajko Nenadov.

**(6)** One of my *partition bijection* problems was resolved by Byungchan Kim.

The reason I started collecting these links is kind of interesting. I was very impressed with George Lusztig and Richard Stanley‘s lengthy writeups about their collected papers that I mentioned in this blog post. While I don’t mean to compare myself to these giants, I figured the casual reader might want to know if a conjecture in some paper had been resolved. Thus the links on my website. I recommend others also do this, as a navigational tool.

#### What gives?

Well, looks like none of my conjectures have been disproved yet. That’s a good news, I suppose. However, by going over my past research work I did discover that on three occasions when I was thinking about other people’s conjectures, I was much too negative. This is probably the result of my general inclination towards “*negative thinking*“, but each story is worth telling.

**( i)** Many years ago, I spent some time thinking about

*Babai’s conjecture*which states that there are universal constants

*C*,

*c*>0, such that for every simple group

*G*and a generating set

*S*, the diameter of the

*Cayley graph*Cay(

*G,S*) is at most

*C*(log |

*G*|)

^{c}. There has been a great deal of work on this problem, see e.g. this paper by Sean Eberhard and Urban Jezernik which has an overview and references.

Now, I was thinking about the case of the symmetric group trying to apply *arithmetic combinatorics* ideas and going nowhere. In my frustration, in a talk I gave (Galway, 2009), I wrote on the slides that “there is much less hope” to resolve Babai’s conjecture for *A _{n} *than for simple groups of Lie type or bounded rank. Now, strictly speaking that judgement was correct, but much too gloomy. Soon after, Ákos Seress and Harald Helfgott

**a remarkable quasi-polynomial upper bound in this case. To my embarrassment, they referenced my slides as a validation of the importance of their work.**

*proved*Of course, Babai’s conjecture is very far from being resolved for *A _{n}*. In fact, it is possible that the diameter is always

*O*(

*n*

^{2}). We just have no idea. For simple groups of Lie type or large rank the existing worst case diameter bounds are exponential and much too weak compared to the desired bound. As Eberhard and Jezernik amusingly wrote in the paper linked above, “

*we are still exponentially stupid*“…

**( ii)** When he was my postdoc at UCLA, Alejandro Morales told me about a curious conjecture in this paper (Conjecture 5.1), which claimed that the number of certain nonsingular matrices over the finite field

**F**

*is polynomial in*

_{q}*q*with positive coefficients. He and coauthors proved the conjecture is some special cases, but it was wide open in full generality.

Now, I thought about this type of problems before and was very skeptical. I spent a few days working on the problem to see if any of my tools can disprove it, and failed miserably. But in my stubbornness I remained negative and suggested to Alejandro that he should drop the problem, or at least stop trying to prove rather than disprove the conjecture. I was wrong to do that.

Luckily, Alejandro ignored my suggestion and soon after ** proved **the polynomial part of the conjecture together with Joel Lewis. Their proof is quite elegant and uses certain recurrences coming from the

*rook theory*. These recurrences also allow a fast computation of these polynomials. Consequently, the authors made a number of computer experiments and

*the positivity of coefficients part of the conjecture. So the moral is not to be so negative. Sometimes you need to prove a positive result first before moving to the dark side.*

**disproved****( iii)** The final story is about the beautiful

*Benjamini conjecture*in probabilistic combinatorics. Roughly speaking, it says that for every finite vertex transitive graph

*G*on

*n*vertices and diameter

*O*(

*n*/log

*n*) the critical percolation constant

*p*

_{c}<1. More precisely, the conjecture claims that there is

*p*<1-ε, such that a

*p*-percolation on

*G*has a connected component of size >

*n*/2 with probability at least δ, where constants ε, δ>0 depend on the constant implied by the

*O*(*) notation, but not on

*n*. Here by “

*p*-percolation” we mean a random subgraph of

*G*with probability

*p*of keeping and 1-

*p*of deleting an edge, independently for all edges of

*G*.

Now, Itai Benjamini is a fantastic conjecture maker of the best kind, whose conjectures are both insightful and well motivated. Despite the somewhat technical claim, this conjecture is quite remarkable as it suggested a finite version of the “*p*_{c}<1″ phenomenon for infinite groups of superlinear growth. The latter is the famous *Benjamini–Schramm conjecture* (1996), which was recently ** proved **in a remarkable breakthrough by Hugo Duminil-Copin, Subhajit Goswami, Aran Raoufi, Franco Severo and Ariel Yadin. While I always believed in that conjecture and even proved a tiny special case of it, finite versions tend to be much harder in my experience.

In any event, I thought a bit about the Benjamini conjecture and talked to Itai about it. He convinced me to work on it. Together with Chis Malon, we wrote a paper proving the claim for some Cayley graphs of abelian and some more general classes of groups. Despite our best efforts, we could not prove the conjecture even for Cayley graphs of abelian groups in full generality. Benjamini noted that the conjecture is tight for products of two cyclic groups, but that justification did not sit well with me. There seemed to be no obvious way to prove the conjecture even for the Cayley graph of *S _{n}* generated by a transposition and a long cycle, despite the very small

*O*(

*n*

^{2}) diameter. So we wrote in the introduction: “In this paper we present a number of positive results toward this unexpected, and, perhaps, overly optimistic conjecture.”

As it turns out, it was us who were being overly pessimistic, even if we never actually stated that we believe the conjecture is false. Most recently, in an amazing development, Tom Hutchcroft and Matthew Tointon **proved **a slightly weaker version of the conjecture by adapting the methods of Duminil-Copin et al. They assume the *O*(*n*/(log* n*)^{c}) upper bound on the diameter which they prove is sufficient, for some universal constant *c*>1. They also extend our approach with Malon to prove the conjecture for all Cayley graphs of abelian groups. So while the Benjamini conjecture is not completely resolved, my objections to it are no longer valid.

#### Final words on this

All in all, it looks like I was never formally wrong even if I was a little dour occasionally (*Yay*!?). Turns out, some conjectures are actually true or at least likely to hold. While I continue to maintain that not enough effort is spent on trying to disprove the conjectures, it is very exciting when they are proved. * Congratulations* to Harald, Alejandro, Joel, Tom and Matthew, and posthumous congratulations to Ákos for their terrific achievements!

## How NOT to reference papers

In this post, I am going to tell a story of one paper and its authors which misrepresented my paper and refused to acknowledge the fact. It’s also a story about the section editor of Journal of Algebra which published that paper and then ignored my complaints. In my usual wordy manner, I do not get to the point right away, and cover some basics first. If you want to read only the juicy parts, just scroll down…

#### What’s the deal with the references?

First, let’s talk about something obvious. *Why do we do what we do?* I mean, why do we study for many years how to do research in mathematics, read dozens or hundreds of papers, think long thoughts until we eventually figure out a good question. We then work hard, trial-and-error, to eventually figure out a solution. Sometimes we do this in a matter of hours and sometimes it takes years, but we persevere. Then write up a solution, submit to a journal, sometimes get rejected (who knew this was solved 20 years ago?), and sometimes sent for revision with various lemmas to fix. We then revise the paper, and if all goes well it gets accepted. And published. Eventually.

So, why do we do all of that? For the opportunity to teach at a good university and derive a reasonable salary? Yes, sure, a to some degree. But mostly because we like doing this. And we like having our work appreciated. We like going to conferences to present it. We like it when people read our paper and enjoy it or simply find it useful. We like it when our little papers form building stones towards bigger work, perhaps eventually helping to resolve an old open problem. All this gives us purpose, a sense of accomplishment, a “social capital” if you like fancy terms.

But all this hinges on a tiny little thing we call citations. They tend to come at the end, sometimes *footnote size* and is the primary vehicle for our goal. If we are uncited, ignored, all hope is lost. But even if we are cited, it matters **how** our work is cited. In what context was it referenced is critically important. Sometimes our results are substantially used in the proof, those are GOOD references.

Yet often our papers are mentioned in a sentence “See [..] for the related results.” Sometimes this happens out of politeness or collegiality between authors, sometimes for the benefit of the reader (it can be hard navigating a field), and sometimes the authors are being self-serving (as in “look, all these cool people wrote good papers on this subject, so my work must also be good/important/publishable”). There are NEUTRAL references – they might help others, but not the authors.

Finally, there are BAD references. Those which refer derogatively to your work, or simply as a low benchmark which the new paper easily improved. Those which say “our bound is terribly weak, but it’s certainly better than Pak’s.” But the WORST references are those which misstate what you did, which diminish and undermine your work.

So for anyone out there who thinks the references are in the back because they are not so important – think again. They are of utmost importance – they are what makes the system work.

#### The story of our paper

This was in June 1997. My High School friend Sergey Bratus and I had an idea of recognizing the symmetric group *S _{n}* using the Goldbach conjecture. The idea was nice and the algorithm was short and worked really fast in practice. We quickly typed it up and submitted to the

*Journal of Symbolic Computations*in September 1997. The journal gave us a lot of grief. First, they refused to seriously consider it since the Goldbach conjecture in referee’s words is “not like the Riemann hypothesis“, so we could not use it. Never mind that it was checked for

*n<10*, covering all possible values where such algorithm could possibly be useful. So we rewrote the paper by adding a variation based on the ternary Goldbach conjecture which was known for large enough values (and now proved in full).

^{14}The paper had no errors, resolved an open problem, but the referees were unhappy. One of them requested we change the algorithm to also work for the alternating group. We did. In the next round the same or another requested we cover the case of unknown *n*. We did. In the next round one referee requested we make a new implementation of the algorithm, now in GAP and report the results. We did. Clearly, the referees did not want our paper to get published, but did not know how to say it. Yet we persevered. After 4 back and forth revisions the paper more than doubled in size (completely unnecessarily). This took two years, almost to the day, but the paper did get accepted and published. Within a year or two, it became a standard routine in both GAP and MAGMA libraries.

**[0]** Sergey Bratus and Igor Pak, Fast constructive recognition of a black box group isomorphic to *S _{n}* or

*A*using Goldbach’s Conjecture,

_{n}*J. Symbolic Comput.*29 (2000), 33–57.

Until a few days ago I never knew what was the problem the referees had with our paper. Why did a short, correct and elegant paper need to become long to include cumbersome extensions of the original material for the journal to accept it? I was simply too inexperienced to know that this is not the difference in culture (CS vs. math). Read on to find out what I now realized.

#### Our competition

After we wrote our paper, submitted and publicized on our websites and various conferences, I started noticing strange things. In papers after papers in Computational Group Theory, roughly a half would not reference our paper, but would cite another paper by 5 people in the field which apparently was doing the same or similar things. I recall I wrote to the authors of this competitive paper, but they wrote back that the paper is not written yet. To say I was annoyed was to understate the feeling.

In one notable instance, I confronted Bill Kantor (by email) who helped us with good advice earlier. He gave an ICM talk on the subject and cited a competition paper but not ours, even though I personally showed him the submitted preprint of [0] back in 1997, and explained our algorithm. He replied that he did not recall whether we sent him the paper. I found and forwarded him my email to him with that paper. He replied that he probably never read the email. I forwarded him back his reply on my original email. Out of excuses, Kantor simply did not reply. You see, the calf can never beat the oak tree.

Eventually, the competition paper was published 3 years after our paper:

**[1]** Robert Beals, Charles Leedham-Green, Alice Niemeyer, Cheryl Praeger, Ákos Seress, A black-box group algorithm for recognizing finite symmetric and alternating groups. I, *Trans. AMS* 355 (2003), 2097–2113.

The paper claims that the sequel II by the same authors is forthcoming, but have yet to appear. It was supposed to cover the case of unknown *n*, which [0] was required to cover, but I guess the same rules do not apply to [1]. Or maybe JSC is more selective than TAMS, one never knows… The never-coming sequel II will later play a crucial part in our story.

Anyhow, it turns out, the final result in [1] is roughly the same as in [0]. Although the details are quite different, it wasn’t really worth the long wait. I quote from [1]:

The running time of constructive recognition in [0] is about the same.

The authors then show an incredible dexterity in an effort to claim that their result is better somehow, by finding minor points of differences between the algorithms and claiming their importance. For example, take look at this passage:

The paper [0] describes the case

G = S, and sketches the necessary modifications for the case_{n}G = A. In this paper, we present a complete argument which works for both cases. The case_{n}G = Ais more complicated, and it is the more important one in applications._{n}

Let me untangle this. First, what’s more “important” in applications is never justified and no sources were cited. Second, this says that BLNPS either haven’t read [0] or are intentionally misleading, as the case of *A _{n}* there is essentially the same as

*S*, and the timing is off by a constant. On the other hand, this suggests that [1] treats

_{n}*A*in a substantively more complicated way than

_{n}*S*. Shouldn’t that be an argument in favor of [0] over [1], not the other way around? I could go on with other similarly dubious claims.

_{n}#### The aftermath

From this point on, multiple papers either ignored [0] in favor of [1] or cited [0] pro forma, emphasizing [1] as the best result somehow. For example, the following paper with 3 out of 5 coauthors of [1] goes at length touting [1] and never even mentioned [0].

**[2]** Alice Niemeyer, Cheryl Praeger, Ákos Seress, Estimation Problems and Randomised Group Algorithms, *Lecture Notes in Math.* 2070 (2013), 35–82.

When I asked Niemeyer as to how this could have happened, she apologized and explained: “The chapter was written under great time pressure.”

For an example of a more egregious kind, consider this paper:

**[3]** Robert Beals, Charles Leedham-Green, Alice Niemeyer, Cheryl Praeger, Ákos Seress, Constructive recognition of finite alternating and symmetric groups acting as matrix groups on their natural permutation modules, *J. Algebra* 292 (2005), 4–46.

They unambiguously claim:

The asymptotically most efficient black-box recognition algorithm known for

Aand_{n}Sis in [1]._{n}

Our paper [0] is not mentioned anywhere near, and cited pro forma for other reasons. But just two years earlier, the exact same 5 authors state in [1] that the timing is “about the same”. So, what has happened to our algorithm in the intervening two years? It slowed down? Or perhaps the one in [1] got faster? Or, more plausibly, BLNPS simply realized that they can get away with more misleading referencing at JOA, than TAMS would ever allow?

Again, I could go on with a dozen other examples of this phenomenon. But you get the idea…

#### My boiling point: the 2013 JOA paper

For years, I held my tongue, thinking that in the age of Google Scholar these self-serving passages are not fooling anybody, that anyone interested in the facts is just a couple of clicks away from our paper. But I was naive. This strategy of ignoring and undermining [0] eventually paid off in this paper:

**[4]** Sebastian Jambor, Martin Leuner, Alice Niemeyer, Wilhelm Plesken, Fast recognition of alternating groups of unknown degree, *J. Algebra* 392 (2013), 315–335.

The abstract says it all:

We present a constructive recognition algorithm to decide whether a given black-box group is isomorphic to an alternating or a symmetric group without prior knowledge of the degree. This eliminates the major gap in known algorithms, as they require the degree as additional input.

And just to drive the point home, here is the passage from the first paragraph in the introduction.

For the important infinite family of alternating groups, the present black-box algorithms [0], [1] can only test whether a given black-box group is isomorphic to an alternating or a symmetric group of a particular degree, provided as additional input to the algorithm.

Ugh… But wait, our paper [0] they are citing already HAS such a test! And it’s not like it is hidden in the paper somehow – Section 9 is titled “What to do if *n* is not known?” Are the authors JLNP blind, intentionally misleading or simply never read [0]? Or is it the “great time pressure” argument again? What could possible justify such outrageous error?

Well, I wrote to the JLNP but neither of them answered. Nor acknowledged our priority. Nor updated the arXiv posting to reflect the error. I don’t blame them – people without academic integrity simply don’t see the need for that.

#### My disastrous battle with JOA

Once I realized that JLNP are not interested in acknowledging our priority, I wrote to the *Journal of Algebra* asking “what can be done?” Here is a copy of my email. I did not request a correction, and was unbelievably surprised to hear the following from Gerhard Hiss, the Editor of the Section on Computational Algebra of the *Journal of Algebra*:

[..] the authors were indeed careless in this attribution.

In my opinion, the inaccuracies in the paper “Fast recognition of alternating groups of unknown degree” are not sufficiently serious to make it appropriate for the journal to publish a correction.

Although there is some reason for you to be mildly aggrieved, the correction you ask for appears to be inappropriate. This is also the judgment of the other editors of the Computational Algebra Section, who have been involved in this discussion.

I have talked to the authors of the paper Niemeyer et al. and they confirmed that the [sic.] did not intend to disregard your contributions to the matter.

Thus I very much regret this unpleasent [sic.] situation and I ask you, in particular with regard to the two young authors of the paper, to leave it at that.

This email left me floored. So, I was graciously permitted by the JOA to be “*mildly aggrieved*“, but not more? Basically, Hiss is saying that the answer to my question “What can be done?” is NOTHING. Really?? And I should stop asking for just treatment by the JOA out of “regard to the two young authors”? Are you serious??? It’s hard to know where to begin…

As often happened in such cases, an unpleasant email exchange ensued. In my complaint to Michel Broué, he responded that Gerhard Hiss is a “respectable man” and that I should search for justice elsewhere.

In all fairness to JOA, one editor did behave honorably. Derek Holt wrote to me directly. He admitted that he was the handling editor for [1]. He writes:

Although I did not referee the paper myself, I did read through it, and I really should have spotted the completely false statement in the paper that you had not described any algorithm for determining the degree

nofAor_{n}Sin your paper with Bratus. So I would like to apologise now to you and Bratus for not spotting that. I almost wrote to you back in January when this discussion first started, but I was dissuaded from doing so by the other editors involved in the discussion._{n}

Let me parse this, just in case. Holt is the person who implemented the Bratus-Pak algorithm in Magma. Clearly, he read the paper. He admits the error and our priority, and says he wanted to admit it publicly but other unnamed editors stopped him. Now, what about this alleged unanimity of the editorial board? What am I missing? Ugh…

#### What really happened? My speculation, part I. The community.

As I understand it, the Computational Group Theory is small close-knit community which as a result has a pervasive groupthink. Here is a passage from Niemeyer email to me:

We would also like to take this opportunity to mention how we came about our algorithm. Charles Leedham-Green was visiting UWA in 1996 and he worked with us on a first version of the algorithm. I talked about that in Oberwolfach in mid 1997 (abstract on OW Web site).

The last part is true indeed. The workshop abstracts are here. Niemeyer’s abstract did not mention Leedham-Green nor anyone else she meant by “us” (from the context – Niemeyer and Praeger), but let’s not quibble. The 1996 date is somewhat more dubious. It is contradicted by Niemeyer and Prager, who themselves clarified the timeline in the talk they gave in Oberwolfach in mid 2001 (see the abstract here):

This work was initiated by intense discussions of the speakers and their colleagues at the Computational Groups Week at Oberwolfach in 1997.

Anyhow, we accept that both algorithms were obtained independently, in mid-1997. It’s just that we finished our paper [0] in 3 months, while it took BLNPS about 4 years until it was submitted in 2001.

Next quote from Niemeyer’s email:

So our work was independent of yours. We are more than happy to acknowledge that you and Sergey [Bratus] were the first to come up with a polynomial time algorithm to solve the problem [..].

The second statement is just not true in many ways, nor is this our grievance as we only claim that [0] has a practically superior and theoretically comparable algorithm to that in [1], so there is no reason at all to single out [1] over [0] as is commonly done in the field. In fact, here is a quote from [1] fully contradicting Niemeyer’s claim:

The first polynomial-time constructive recognition algorithm for symmetric and alternating groups was described by Beals and Babai.

Now, note that both Hiss, Holt, Kantor and all 5 authors BLNPS were at both the 1997 and the 2001 Oberwolfach workshops (neither Bratus nor I were invited). We believe that the whole community operates by “they made a stake on this problem” and “what hasn’t happened at Oberwolfach, hasn’t happened.” Such principles make it easier for members of the community to treat BLNPS as pioneers of this problem, and only reference them even though our paper was published *before* [1] was submitted. Of course, such attitudes also remove a competitive pressure to quickly write the paper – where else in Math and especially CS people take 4-5 years(!) to write a technically elementary paper? (this last part was true also for [0], which is why we could write it in under 3 months).

In 2012, Niemeyer decided to finally finish the long announced part II of [1]. She did not bother to check what’s in our paper [0]. Indeed, why should she – everyone in the community already “knows” that she is the original (co-)author of the idea, so [4] can also be written as if [0] never happened. Fortunately for her, she was correct on this point as neither the referees nor the handling editor, nor the section editor contradicted false statements right in the abstract and the introduction.

#### My speculation, part II. Why the JOA rebuke?

Let’s look at the timing. In the Fall 2012, Niemeyer visited Aachen. She started collaborating with Professor Plesken from RWTH Aachen and his two graduate students: Jambor and Leuner. The paper was submitted to JOA on December 21, 2012, and the published version lists affiliation of all but Jambor to be in Aachen (Jambor moved to Auckland, NZ before the publication).

Now, Gerhard Hiss is a Professor at RWTH Aachen, working in the field. To repeat, he is the Section Editor of JOA on Computational Algebra. Let me note that [4] was submitted to JOA three days before Christmas 2012, on the same day (according to a comment I received from Eamonn O’Brien from JOA editorial board), on which apparently Hiss and Niemeyer attended a department Christmas party.

My questions: is it fair for a section editor to be making a decision contesting results by a colleague (Plesken), two graduate students (Jambor and Leuner), and a friend (Niemeyer), all currently or recently from his department? Wouldn’t the immediate recusal by Editor Hiss and investigation by an independent editor be a more appropriate course of action under the circumstances? In fact, this is a general Elsevier guideline if I understand it correctly.

#### What now?

Well, I am at the end of the line on this issue. Public shaming is the only thing that can really work against groupthink. To spread the word, please LIKE this post, REPOST it, here on WP, on FB, on G+, forward it by email, or do wherever you think appropriate. Let’s make sure that whenever somebody googles these names, this post comes up on top of the search results.

P.S. Full disclosure: I have one paper in the *Journal of Algebra*, on an unrelated subject. Also, I am an editor of *Discrete Mathematics*, which together with JOA is owned by the same parent company *Elsevier*.

UPDATE (September 17, 2014): I am disallowing all comments on this post as some submitted comments were crude and/or offensive. I am however agreeing with some helpful criticism. Some claimed that I crossed the line with some personal speculations, so I removed a paragraph. Also, Eamonn O’Brien clarified for me the inner working of the JOA editorial board, so removed my incorrect speculations on that point. Neither are germane to my two main complaints: that [0] is repeatedly mistreated in the area, most notably in [4], and that Editor Hiss should have recused himself from handling my formal complaint on [4].

UPDATE (October 14, 2014): In the past month, over 11K people viewed this post (according to the WP stat tools). This is a simply astonishing number for an inactive blog. Thank you all for spreading the word, whether supportive or otherwise! Special thanks to those of you in the field, who wrote heartfelt emails, also some apologetic and some critical – this was all very helpful.