Is it fair to desk-reject a manuscript because it breaks relativity?

Question

Every so often a journal I edit receives papers with some kind of claim that, if true, would break mainstream physics. For example, a paper could claim that waves in dark matter can travel at v ~ 10¹⁴ m/s.

Because relativity has met every experimental test we've thrown at it, and because relativity has a hard limit on velocities at the speed of light (3×10⁸ m/s), any paper making this kind of claim is immediately suspect. One doesn't need to know what else is in the paper to be pretty confident it is wrong.

However, it is also known that relativity is an incomplete theory because it is incompatible with quantum mechanics. It's conceivable that whatever theory eventually supplants these two theories could allow velocities greater than the speed of light.

Question: Is it fair to desk-reject the above paper based solely on this one sentence? Like, there's a 99.99% chance (maybe even higher) that the paper is wrong, but there's still a nonzero chance it could be correct. If it is unfair, what else do I need before it becomes fair to desk-reject?

Answer 1

That procedure would remove the ability to overturn incorrect mainstream results. But the author should explicitly address the issue

Whilst I appreciate the Bayesian reasoning involved here (high a priori probability of invalidity), the suggested process has the drawback that it could never allow publication of a correct idea that overturns an established (but false) rule of physics. As you say, it is contrary to "mainstream" physics, which is usually, but perhaps not necessarily, synonymous with correct physics. Ideally, the peer review process ought to operate on the merits of ideas and arguments rather than dismissing them without review if they are contrary to the "mainstream". This would allow challenges to the mainstream view to be considered on the merits, and would mean that it is possible for incorrect positions in the mainstream view to be overturned with peer reviewed literature. Moreover, even when the mainstream position is correct, exposure to a plausible alternative view or critique could sharpen the mainstream position.

Obviously this has a time cost, but hopefully a reasonably modest one. Desk rejection requires a desk review, so I think it would be wrong to reject on the basis of that one sentence, notwithstanding that it makes an assertion that is contrary to mainstream physics. Ideally, the initial editor should undertake an initial review of the paper to see if it is understandable, and may make a positive contribution to the literature. If it provides novel results, is understandable, and you can't see any critical flaw that would invalidate it (even if you think there must be one, because the result is implausible), then it is probably a candidate to proceed to referee review, or at least a more comprehensive deep-dive review by the initial editor. For a deeper review, obviously one of the things you are going to look for is for the author to provide an explanation of the implications and counter-arguments to their position. If the result would indeed "break" mainstream physics, then it would behove the author to give some explanation of how to resolve the breakage, or in what position that leaves the field (e.g., are the empirical results in other literature still correct, but for another reason, or are they incorrect for some reason).** It might be useful if you have a few referees available who are happy to take on reviews of "implausible results" and have the patience to look deeply into the arguments, notwithstanding the implausibility of the conclusion.

One reason that you might legitimately desk reject a paper of this kind is if a claim made tangentially in the paper so fundamentally contradicts an established law of physics that that claim ought to be the topic of the paper. For example (hat tip to Peter Schneider in comments), for an assertion that a thing travels faster than the speed of light, that would be a major discovery in itself (with large implications), and it ought to be the topic of the paper. If it is mentioned only tangentially as an aspect of study of something less important then that is a serious deficiency of the paper, and may warrant rejection (with an instruction to the author to check if the result is correct, and if so, write the ground-breaking paper focused on that result).

One of the reasons I take this position is that one of the critiques one sometimes hears of academic peer review is that it is a closed shop that assesses ideas based on popularity rather than merit. Adopting the procedure you are suggesting seems to me to go down the avenue of validating this type of critique --- a paper is immediately dismissed because it makes a claim that is not "mainstream". (This criticism of academia is not entirely without merit, but I'd hope that the procedures of peer review would mean it is a marginal phenomenon at most; we certainly shouldn't be adopting practices that explicitly incorporate an initial rejection criterion for results that contradict mainstream understanding.)

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Update (10 April 2023): In relation to this topic, you might be interested in a recent case where a published paper asserted a result that called standard physics models into question, only to be subsequently questioned itself as potentially erroneous. Aaltonen et al (2022) analysed a 2011 dataset from a large hadron collider at CDF to infer the weight of the W-Boson. The paper found it to be substantially heavier than expected under the standard model of this type of particle (see related report here), which would have implications for whether there are additional hidden objects that are not in the standard model. However, CDF researchers examining the same dataset with an alternative statistical model find that the inferred weight is in accordance with standard model, and think that the unusual result may be due to inadequate statistical modelling (see report here). This episode is somewhat similar to the issue you raise here, and it looks like it is a case of inadequate statistical modelling causing a published "world breaking" result. Even assuming that the original published paper turns out to be wrong, there may be some residual value from having both published analyses of the data, since they show the effect of better specification of the statistical model for the data.

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** Don't be too demanding here on resolving the breakage --- finding an error in mainstream understanding of the discipline doesn't mean you know all the implications just yet, but the author should at least address the issue, outline their understanding of the implications, and respond to obvious counter-arguments.

Answer 2

If they don't address the issue in the paper or claim this suggests an issue with their assumptions that should be addressed in future work then I'd say it’s fair. In addition, this is an extraordinary claim and so there should be some extraordinary evidence/reason to accept it, though experimental work might have a lower threshold than theory to avoid a desk reject.

Don't forget, to not give a desk reject to a paper that has clear issues with it is unfair to the reviewers since they will probably just come back with the same issue you had initially, but they have now wasted time reading the article.

It’s also possible they had a typo in the paper such as the number really being v^2 or got the exponent wrong where it should have been 10^4 rather than 10^14. If you are worried about the desk reject being unfair you could perhaps ask the authors for clarification or make the reason very clear during the reject so that if there was a mistake then it’s very easy for the authors to contest the desk reject in an appeal (depending on your journal's policies).

Answer 3

My suggested approach can be summed up with Sagan's standard:

Extraordinary claims require extraordinary evidence.

Or rather, Laplace's original formulation:

The weight of evidence for an extraordinary claim must be proportioned to its strangeness.

Note that the maxim is not "Extraordinary claims should be desk rejected to save everyone time, because they're almost certainly wrong". They are almost certainly wrong, but there's a non-zero chance they might be true, which is why they need the proportionate amount of evidence to back them up.

If an author is submitting a paper which makes an extraordinary claim (e.g. that relativity is broken), it's incumbent on that author to provide the extraordinary evidence that it's not a whole lot of hogwash -- that is, to provide sufficient evidence that the claim is valid. It's your job as an editor to provide the first-pass assessment of the provided evidence, and see if the extraordinary-ness of the evidence is proportioned to the extraordinary-ness of the claim.

How much evidence is needed is somewhat topic and field specific. As mentioned, the needed evidence is proportional to the strangeness of the claim. The more fringe and unexpected the claim, the more effort the author needs to go through to prove that the claim is valid.

Generally speaking, a decent scientist who knows the claim is extraordinary (and who ascribes to Sagan's standard) will put in the effort to back up the claim. It will be rather obvious that they're doing their best to back things up. (They will make some effort in that regard.) On the other hand, if someone is not aware that the claim is extraordinary, or if they don't care about the standard (e.g. if they're a crank), the paper will be tissue-paper thin on the point. In these latter cases you can safely desk reject with a note they'll need to spend effort backing up their claim.

Answer 4

Uhlenbeck and Goudsmit introduced the electron spin in a model that would require the electron to spin faster than the speed of light. Yet they were right although their model of a classically spinning electron was wrong.

So: breaking relativity should not lead to an immediate reject.

The story of this “error” can be found in

Electron Spin and Its History, Eugene D. Commins, Annual Review of Nuclear and Particle Science 2012 62:1, 133-157

and available here. The salient part (with relevant actors properly identified) is as follows:

Discouraged by Lorentz's criticism, Uhlenbeck and Goudsmit told Ehrenfest that they wished to withdraw their paper. However, Ehrenfest had already sent it to the publisher. He told Uhlenbeck and Goudsmit not to worry: They were young enough to be forgiven for their stupidity! The short paper was published in Naturwissenschaften in November 1925 (13), and an even shorter version, in English, appeared in Nature in February 1926 (14).

Answer 5

One should be very clear about what it exactly means that a theory violates Special Relativity (SR), because there exist at least three classes of situations where "violations" of SR are harmless.

1. In relativistic quantum mechanics, the magnitude <x| \exp{-iHt} |x=0> of a free particle is positive definite everywhere. So the particle can be located, with some probability, outside its forward light cone. Does this violate SR mathematically? Yes, big time. Does it violate SR in actual physical experiments? No way. Because it is impossible to localise a particle to volumes less than the Compton wavelength λ. (Such an attempt would boost the energy uncertainty and generate a multi-particle state.) In short, a single-particle theory is inconsistent with the SR causality. Thus, if a violation of SR happens within a less-than-Compton volume, it may be ignored. For it will not enable you to send superluminal signals.

2. Similar is the situation with quantum entanglement. Does the entanglement violate SR mathematically? Sure. Does it violate SR in real life? Never. Because quantum entanglement does not enable superluminal signal transmission.

3. In cosmology, inflation permits for patches of the manifold to recede from one another faster than light. This, however, does not imply superluminal signal exchange.

To conclude, we should be tolerant to the violations of SR that are purely mathematical.

If I were an editor, I would ask the authors of SR-violating theories the same question: does the "violation" imply the possibility of superluminal exchange over longer-than-Compton scales? If no, then the theory can be considered for publication. If yes -- then the author must, at the very least, discuss the extent of the violation, and its consequences.

Answer 6

As mentioned in comments, phase velocities exceeding c are perfectly normal in relativistic wave theories. Group velocities can also exceed c when there is anomalous dispersion. Recessional velocities in cosmology can also exceed c. Without context, it's not clear whether the claim in the paper is related to any of those, but I hope that before rejecting the paper you'll consider the possibility that the claim isn't as extraordinary as you think.

Of course, the authors should make that clear. But if they mention that the velocity is a phase velocity, or mention anomalous dispersion, I wouldn't expect them also to say that it doesn't violate causality, since the intended audience would understand that. I think the paper wouldn't be improved by adding an explicit disclaimer in those cases.

Answer 7

I don't do physics, but if I, as editor, come across results that look implausible, my first impulse is to see how good the rest of the paper looks; in most (or even all, see below) such cases I easily find other issues and then I have a good basis to desk reject. One sentence alone shouldn't be enough if the thing looks well done otherwise. If I remember correctly, I never needed to reject a paper based on one implausible result alone; there was always more to be found.

Answer 8

No, this isn't a situation in which a desk reject is appropriate unless the editor can see a fatal flaw in the paper themself. It is actually, in that case, a situation in which you bring in the "big guns" to look at the arguments.

There is a misconception by many, possibly including some editors, that the "real world" somehow conforms to or obeys a set of theories. In fact the real world is what it is and our theories, including relativity, are just our (feeble) attempts to understand and explain that within a theoretical/computable/mathematical context.

The fact that "all available evidence" (if true) supports relativity doesn't mean that there isn't some better, more inclusive theory in which it sometimes fails. Don't suppose that "all available evidence" is the same as "all evidence". We haven't, certainly been able to examine all possible phenomena in such a complex world. It is hubris to assume otherwise.

In particular we have lots of limits on what is visible to us, both at micro and macroscopic scale. Likewise on long and short term time scales.

Of course, an editor would/should be skeptical of claims made in such papers and errors can be missed by the best researchers, but there is still a lot to be examined and understood about the real world. Not all possible phenomena are apparent to us. That is one reason that it took Einstein about ten years to come up with (even) special relativity and he did so in the face of opposition of the scientific establishment of the time, who were pretty generally committed to the theory of the aether. And his results weren't IIRC immediately endorsed and accepted by all.

Big world.

Quoting from Wikipedia

Galileo's championing of Copernican heliocentrism (Earth rotating daily and revolving around the Sun) was met with opposition from within the Catholic Church and from some astronomers. The matter was investigated by the Roman Inquisition in 1615, which concluded that heliocentrism was foolish, absurd, and heretical since it contradicted Holy Scripture.

Don't do that.

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Yes, I do realize that the Inquisition of 1615 were, indeed, the big guns of the day. Oh well.

Answer 9

I am not sure there is a one-size-fits-all answer to your question. There are different journals with different policies, some journals have more appetite to speculative ideas than others. I doubt one should think about desk rejections in terms of fair/unfair. Desk rejections (or maybe any editorial decisions) always carry the risk of an error, but many (or maybe most) journals cannot do without desk rejections. There are a lot of journals nowadays, and an author should not be too thin-skinned and give up after a rejection.

Let me refer you to Gell-Mann's views in (a very short) https://www.youtube.com/watch?v=GSLY2ojYZHg , where he criticizes the policies of Phys. Rev. and Phys. Rev. Lett. Apparently, his letters to these journals were not always met enthusiastically :-), so he tended to publish elsewhere. Was Phys. Rev. unfair to Gell-Mann? I don't think so, they just had policies that he disliked (and I am not trying to say that Phys. Rev. was right and Gell-Mann was wrong, or vice versa).

Answer 10

Is it fair to desk-reject the above paper based solely on this one sentence?

My claim: Under no circumstances, is it fair to reject heretic claims based on their contrarianism alone, without going through the reasoning. It may still have to be done due to other constraints of time and effort, but it is never fair.

May I request you to have a look at three case studies that I have compiled to beg reconsideration of the antithetical expression established knowledge. The point is that contrarian claims should never be discarded solely on the basis of their contrarianism alone. These historical examples emphasize that the presumption of established knowledge can be unfair to contrarian thinkers.

The following three counter-examples are a case in point as to why desk rejection mainly because of heresy may not be a good idea. It only intends to provide a proof by counterexamples; to complement other answers which are well written and cover all of the important points.

Evidence

Case 1: Pulsars

Thomas Gold (1920 - 2004) was a brilliant contrarian scientist and a professor emeritus in the Department of Astronomy at Cornell University.

As a consultant to NASA in 1955, Gold conjectured that "the Moon is covered by a layer of dust resulting from the ceaseless bombardment of its surface by Solar System debris" (Bondi 2004). He was opposed by many of his colleagues, but was eventually proven right when the crew of Apollo 11 returned with samples of lunar rock and regolith in 1969.

Astronomer Jocelyn Bell Burnell along with her doctoral adviser Antony Hewish (1924 - 2021) discovered a regularly pulsating source of radio waves in the sky with a pulse width of 0.3 seconds and a period of 1.337 seconds, later called as a pulsar (Hewish 1968). Thomas Gold hypothesized that pulsars are vigorously spinning neutron stars emitting radio waves from their magnetic poles (Gold 1969). This was considered so outrageous that he, a Cornell University astronomer and a NASA consultant, was not even permitted to present it at the first international conference on pulsars (Dermott 2004). This incident begs the following question: Is any idea ever outrageous enough to exceed the outrage of not allowing the idea to be talked about in the first place?

The experience of Thomas Gold is not uncommon. Contrarian thinkers challenging the consensus narrative have always faced unfair, sharp, and inconsiderate rejection from the mainstream thinker community as well as the public at large.

Case 2: Rogue Waves

For centuries, sailors had reported witnessing extremely large, sudden waves, over 30 meters high, that seemed to come out of nowhere. Such waves became known as rogue waves or monster waves. Scientists almost universally believed the rogue waves to be a myth for hundreds of years.

When the renowned and respected explorer Jules Dumont d’Urville (1790 - 1842) confirmed experiencing such waves in his expeditions, which was corroborated by his co-travelers, it was ridiculed even by the then French Prime Minister François Arago (1786 - 1853) who was also a well respected scientist and mathematician (Levine 2018).

In 1994, the Draupner E oil drilling platform was constructed in the North Sea, 160 kilometers off the coast of Norway. It was designed to withstand waves of 20 meters height, estimated at that time to occur once every 10,000 years (Levine 2018). On 1st January 1995, the platform was hit by a 26 meter high wave in a relatively calm sea with no storm in the vicinity, thus conclusively establishing the existence of rogue waves. It is now believed that rogue waves are much more common than previously thought, with many of the strange unexplained maritime incidents in history now being hypothesized as having been caused due to rogue waves (Groch 2022).

Case 3: Quasicrystals

Dan Shechtman (born 1941), a professor of materials science at the Israel Institute of Technology, was studying rapidly solidified alloys of aluminum with the transition metals, a major class of metals based on their chemical properties. He discovered quasicrystals in 1984 while on a sabbatical at the John Hopkins University.

It was believed at that time that the solid state of matter can show only two fundamentally distinct states of arrangements of the molecules: crystalline and amorphous. In the amorphous solids, like glass for example, the arrangement of the molecules is aperiodic and disordered. Aperiodic means that the pattern does not repeat itself over space; disordered means that there are no simple rules governing the pattern, meaning that the unseen portions of the pattern cannot be predicted over a significant range. In the crystalline solids, the arrangement of molecules is periodic and ordered, meaning that it is repetitive and predictable.

The quasicrystalline state of arrangement of molecules, discovered by Shechtman, is characterized by patterns that are ordered, but aperiodic. In other words, the arrangement of molecules is predictable, but not repetitive. It was an unexpected discovery, and Shechtman faced enormous backlash from the scientific community.

The paper describing his research findings was repeatedly rejected, getting published only after more than two years. After the publication, the head of his research group at the John Hopkins University called him a disgrace to the group and asked him to leave (Jha 2013). Linus Pauling (1901 – 1994), a strong contender for the title of the greatest chemist ever, one of the founders of quantum chemistry and molecular biology, strongly rejected Shechtman’s findings, saying, "There are no quasi-crystals, just quasi-scientists" (Jha 2013). Shechtman was eventually vindicated and even won the Nobel Prize for Chemistry in 2011.