The disappointing story of superconductivity in Strontium Ruthenate

In 1994 superconductivity was discovered in strontium ruthenate (Sr2RuO4). This attracted considerable interest because it had a perovskite crystal structure, just like the cuprates. Furthermore, it was a stoichiometric compound and so not plagued by impurities like the cuprates.

In 1998, things got more interesting when NMR Knight shift measurements were interpreted as evidence for triplet superconductivity.

Analogues were made with triplet Cooper pairing in superfluid 3He mediated by ferromagnetic spin fluctuations.

Triplet pairing is associated with odd-parity (spatial) and time-reversal symmetry breaking. Evidence for the latter was claimed from muon spin relaxation (muSR) and the polar Kerr effect.

There are subtle questions about whether a bulk sample of a triplet superconductor exhibits spontaneous magnetisation. Leggett discussed this in an Appendix of his textbook. It turns out the magnetisation probably only exists on the edges.

Aside. The metallic phase is of interest because (unlike the cuprates) it is a Fermi liquid. More recently, it has been argued to be a Hund's metal.

Fueled by hype about topological quantum computing, the past two decades have seen even greater interest in the material due to proposals that it may be a topological superconductor. See for example, this paper.

Now we come to the disappointment. It turns out that the original Knight shift measurements were flawed, probably due to a problem with thermometry.

Recent, careful Knight shift measurements suggest spin-singlet pairing. They were described in a Physics Today article by Alex Lopatka in 2021, An unconventional superconductor isn’t so odd after all. The article describes all the intricacies and challenges of these measurements. Stuart Brown is to be commended for persisting with this problem.

What about the Kerr effect and muSR measurements suggesting time-reversal symmetry breaking?

The polar Kerr effect involves rotation of the plane of polarisation of the electromagnetic radiation by an angle of 65 nanoradians! There is only one group in the world (at Stanford) that can detect these ultra-minute rotations.

muSR may also be problematic. It is not really known where the implanted muon sits in the crystal or what effect it has on the surrounding crystal structure. In particular, these perturbations may produce a small local magnetic field which is nothing to do with the claimed global field due to the magnetism associated with the triplet superconductivity. A recent preprint by Warren Pickett considers some of the challenges associated with interpreting these experiments as evidence for time-reversal symmetry breaking.

What is disappointing about this?

Obviously, it would be nice to have a triplet superconductor and even more a topological one.

However, for me, the big disappointment is that it took almost thirty years for the original NMR measurements to be checked and shown to be wrong. This may reflect several sociological problems.

Kauzmann's maxim: people will tend to believe what they want to believe rather than what the evidence before them might suggest.

The condensed matter community tends to be infatuated with exotica.

There is not enough application of Occam's razor. Luxury journals don't want simple explanations or authors to raise doubts or ambiguities.

As far as I am aware, the 1998 Nature paper on the NMR Knight shift has still not been retracted.

This post was stimulated by a helpful colloquium at UQ given recently by James Annett. He has worked on strontium ruthenate for many years and is a co-author of a relevant review article.

Update. 23 April. James Annett pointed out to me that the authors for the 1998 NMR published a paper in 2020 which acknowledges that their original paper was incorrect.

Reduction of the 17O Knight Shift in the Superconducting State and the Heat-up Effect by NMR Pulses on Sr2RuO4

Wading through AI hype about materials discovery

 Discovering new materials with functional properties is hard, very hard. We need all the tools we can from serendipity to high-performance computing to chemical intuition. 

At the end of last year, two back-to-back papers appeared in the luxury journal Nature.

Scaling deep learning for materials discovery

All the authors are at Google. They claim that they have discovered more than two million new materials with stable crystal structures using DFT-based methods and AI.

On Doug Natelson's blog there are several insightful comments on the paper about why to be skeptical about AI/DFT based "discovery".

Here are a few of the reasons my immediate response to this paper is one of skepticism.

It is published in Nature. Almost every "ground-breaking" paper I force myself to read is disappointing when you read the fine print.

It concerns a very "hot" topic that is full of hype in both the science and business communities.

It is a long way from discovering a stable crystal to finding that it has interesting and useful properties.

Calculating the correct relative stability of different crystal structures of complex materials can be incredibly difficult.

DFT-based methods fail spectacularly for the low-energy properties of quantum materials, such as cuprate superconductors. But, they do get the atomic structure and stability correct, which is the focus of this paper.

It is a big gap between discovering a material that has desirable technological properties to one that meets the demanding criteria for commercialisation.

The second paper combines AI-based predictions, similar to the paper above, with robots doing material synthesis and characterisation.

An autonomous laboratory for the accelerated synthesis of novel materials

[we] realized 41 novel compounds from a set of 58 targets including a variety of oxides and phosphates that were identified using large-scale ab initio phase-stability data from the Materials Project and Google DeepMind

These claims have already been undermined by a preprint from the chemistry departments at Princeton and UCL.

Challenges in high-throughput inorganic material prediction and autonomous synthesis

We discuss all 43 synthetic products and point out four common shortfalls in the analysis. These errors unfortunately lead to the conclusion that no new materials have been discovered in that work. We conclude that there are two important points of improvement that require future work from the community: 

(i) automated Rietveld analysis of powder x-ray diffraction data is not yet reliable. Future improvement of such, and the development of a reliable artificial intelligence-based tool for Rietveld fitting, would be very helpful, not only to autonomous materials discovery, but also the community in general.

(ii) We find that disorder in materials is often neglected in predictions. The predicted compounds investigated herein have all their elemental components located on distinct crystallographic positions, but in reality, elements can share crystallographic sites, resulting in higher symmetry space groups and - very often - known alloys or solid solutions. 

Life is messy. Chemistry is messy. DFT-based calculations are messy. AI is messy. 

Given most discoveries of interesting materials often involve serendipity or a lot of trial and error, it is worth trying to do what the authors of these papers are doing. However, the field will only advance in a meaningful way when it is not distracted and diluted by hype and authors, editors, and referees demand transparency about the limitations of their work.  

Majorana: mysterious disappearance of a particle and of credibility

The theoretical physicist Ettore Majorana mysteriously disappeared in 1938. Unfortunately, Majorana particles are also going to be associated in history with some mysterious disappearances: their own existence, the prospect of a topological quantum computer, some prominent scientists' reputations, and the credibility of Physical Review journals.

Nine years ago I expressed skepticism that there would ever be a quantum computer based on Majorana fermions. I wish I was wrong. It certainly would be cool. Things are even worse than I thought. The issues (scientific, ethical, technological, hype, ...) were recently highlighted in a strange incident involving a paper from Microsoft that was published by PRB.

I found the commentary of Vincent Mourik on the whole incident enlightening and disturbing. His description is "Here's the full background of my involvement with the recent Microsoft Quantum paper. APS pulled off an arcane unofficial off-the-record peer review already one year ago when it was presented at PRX. And then published it anyway at PRB..."

I do have concerns about the unusual practice used by PRX and the precedent of publishing a paper with incomplete details. However, my more significant concern is that, based on Vincent's report, this paper should never have been published in any self-respecting scientific journal. I fear that in order to "compete" with the luxury journals Physical Review has descended to their low scientific and ethical standards.

I thank Doug Natelson and a commenter on his blog for bringing this sorry saga to my attention.

Systemic flaws that are undermining good science

Everyone likes to be right. But, sometimes I really wish I was wrong, particularly about problems I see in the world. I wish I was wrong about science being broken. Some of these issues I discuss in the final chapter of Condensed Matter Physics: A Very Short Introduction, due to the relevance of these problems to the future of the field.

Similar concerns were discussed with greater clarity, way back in 2014, by four scientists who are much more experienced and distinguished than I am. 

Rescuing US biomedical research from its systemic flaws 

Bruce Alberts, Marc W. Kirschner, Shirley Tilghman, and Harold Varmus

Positions the different authors have held include President of the US Academy of Sciences, President of Princeton University, and Director of the National Institutes of Health.

Although the article focuses on biomedical research I think the three words "medicine, biomedical, and biology" could be replaced respectively with "technology, materials science, and condensed matter physics" almost everywhere in the article. 

Here are a few quotes.

The long-held but erroneous assumption of never-ending rapid growth in biomedical science has created an unsustainable hypercompetitive system that is discouraging even the most outstanding prospective students from entering our profession—and making it difficult for seasoned investigators to produce their best work. This is a recipe for long-term decline, and the problems cannot be solved with simplistic approaches. Instead, it is time to confront the dangers at hand and rethink some fundamental features of the US biomedical research ecosystem.

... the remarkable outpouring of innovative research from American laboratories—high-throughput DNA sequencing, sophisticated imaging, structural biology, designer chemistry, and computational biology—has led to impressive advances in medicine and fueled a vibrant pharmaceutical and biotechnology sector. In the context of such progress, it is remarkable that even the most successful scientists and most promising trainees are increasingly pessimistic about the future of their chosen career.

... hypercompetition for the resources and positions that are required to conduct science suppresses the creativity, cooperation, risk-taking, and original thinking required to make fundamental discoveries.

The system now favors those who can guarantee results rather than those with potentially path-breaking ideas that, by definition, cannot promise success. Young investigators are discouraged from departing too far from their postdoctoral work, when they should instead be posing new questions and inventing new approaches. Seasoned investigators are inclined to stick to their tried-and-true formulas for success rather than explore new fields. 

One manifestation of this shift to short-term thinking is the inflated value that is now accorded to studies that claim a close link to medical practice. Human biology has always been a central part of the US biomedical effort... Many surprising discoveries, powerful research tools, and important medical benefits have arisen from efforts to decipher complex biological phenomena in model organisms. In a climate that discourages such work by emphasizing short-term goals, scientific progress will inevitably be slowed, and revolutionary findings will be deferred.

As competition for jobs and promotions increases, the inflated value given to publishing in a small number of so-called “high impact” journals has put pressure on authors to rush into print, cut corners, exaggerate their findings, and overstate the significance of their work. 

The development of original ideas that lead to important scientific discoveries takes time for thinking, reading, and talking with peers. Today, time for reflection is a disappearing luxury for the scientific community. 

...administrative tasks are taking up an ever-increasing fraction of the day and present serious obstacles to concentration on the scientific mission itself. 

The following is particularly true of luxury journals. 

Professional editors are increasingly serving in roles played in the past by working scientists and can undermine the enterprise when they base judgments about publication on newsworthiness rather than scientific quality. 

Even after they have landed a research position in academia or research institutes, new investigators wait an average of 4–5 y to receive federal funding for their work compared with 1 y in 1980 (2). Two stark statistics tell much of the tale—the average age at which PhD recipients assume their first tenure-track job is 37 y, and they are approaching 42 y when they are awarded their first NIH grant.

Although it varies across fields and individuals, I get the impression that most scientists do their best work in the rough age range of 35-45. Currently, people are spending most of these years looking for a permanent job and then applying for grants, rather than actually doing science.

The graph below shows just how much the system changed in just thirty years. NIH grants became "gentrified". In different words, all the grants now go to "old farts" doing the same old thing, rather than to "young turks" who want to try new things and have a real impact.

Percentage of NIH R01 Principal Investigators aged 36 and younger and aged 66 and older, 1980–2010

The authors did make some concrete proposals and in a follow-up article, they discuss a broader meeting held to discuss the issues.

Addressing systemic problems in the biomedical research enterprise

To what extent progress has been made in the biomedical community in the past eight years I do not know.

The science and politics of the origins of covid-19

I want to begin by stating some hypotheses. Some may be obvious. Others may be contentious. I will number them so that people can easily make comments about specific ones. The underlying issues are illustrated in recent debates about the possible origins of covid-19.

1. Systematic critical thinking is essential to scientific progress and public policy. Healthy doses of skepticism can be valuable.

2. Science progresses well by making multiple hypotheses and examining carefully what evidence is consistent with each of the hypotheses. This is something that Murray Gell-Mann wished someone had told him when he was twenty years old.

3. Transparency is essential to science. People need to share data, including primary data. The more that such data is publicly available the better. This is what open science advocates. 

4. Science is built on ethical conduct, both implicit and explicit. It is important that declarations of conflicts of interest are not just a box-ticking exercise.

5. Scientists cannot have allegiance to some greater authority than truth and integrity. Problematic allegiances include to a company, a family, an institution, a political party, or to a nation. An example is the case of the recent change to the charter of Fudan University, indicative of the stranglehold that the Chinese Communist Party has over Chinese universities.

6. Given these issues about integrity and conflicts of interest luxury journals are problematic because there is a conflict of interest between the commercial success of the publisher in the short term (achieved by promoting hype, i.e. newsworthy sexy scientific breakthroughs, even if they are wrong) and the boring work of doing careful painstaking science.

7. One approach to solving some of these problems is self-regulation of scientific communities. However, when sub-communities (e.g. virologists, string theorists) self-regulate this may be impeded by conflicts of interest.

8. Given the issues above, science journalists need to be more critical and skeptical. Too often they seem in awe of scientists and want to promote hype as it sells. Journalists need to ask more hard questions about conflicts of interest, weak reasoning, claimed "breakthroughs", hype, proposed great technological applications, and the "science as saviour" narrative.

9. There is a fear among scientists about publically speaking about scientific uncertainty and ambiguity. This fear is understandably driven by the experience of "skeptics" latching onto uncertain statements to promote climate change denialism, young-earth creationism, and anti-vaccines. Thus, a great challenge in public engagement is to educate about the role of uncertainty in science.

10. Science always occurs in a political context whether it is in Australia, Romania, or China. The context will always have some influence, but it should not be determinative.

11. The greater the stakes (whether potential Nobel Prizes, company profits, government scandal, a disaster) in play, the greater the likelihood will be for mistakes, corruption, deception, and cover-up. Consequently, the level of scientific diligence and regulation needs to be proportionate to the possible benefits and risks. Extraordinary claims require extraordinary evidence.

12. Beware of the argument from authority. A hypothesis should be accepted or rejected based on the quality of the reasoning and evidence provided, not on the scientific prestige (or lack thereof) of the proponent.

All of the claims above I see played out recently in debates about the origins of covid-19. Two distinct hypotheses are dissected in a helpful and long article recently published in the Bulletin of Atomic Scientists.

The origin of COVID: Did people or nature open Pandora’s box at Wuhan?  Nicholas Wade 

Hypothesis 1. The virus spread from a wet market in Wuhan. The virus was zoonotic, i.e. as a result of evolution it crossed the species barrier from bats to humans.

Hypothesis 2. The virus spread from the Wuhan Institute of Virology where a research group was investigating bat viruses and doing "gain of function" research to see how the bat viruses might be modified genetically into a form that could infect humans. 

The article is worth reading because it carefully lays out the science while also raised many of the issues I mention above. A few things that I learned follow.

There is significant evidence that the MERS, SARS1, Ebola viruses are zoonotic. The evidence consists of finding intermediate genetic forms in intermediate species. Often this evidence was found within months of the disease outbreak. In contrast, after 18 months there is still no evidence of intermediate forms for SARS2.

The "gain of function" research in Wuhan was being funded by the USA National Institutes of Health, via a grant to the EcoHealth Alliance of New York, led by Peter Daszak. Wade writes

"We stand together to strongly condemn conspiracy theories suggesting that COVID-19 does not have a natural origin,” a group of virologists and others wrote in the Lancet on February 19, 2020, when it was really far too soon for anyone to be sure what had happened. Scientists “overwhelmingly conclude that this coronavirus originated in wildlife,” they said, with a stirring rallying call for readers to stand with Chinese colleagues on the frontline of fighting the disease.

Contrary to the letter writers’ assertion, the idea that the virus might have escaped from a lab invoked accident, not conspiracy. It surely needed to be explored, not rejected out of hand. A defining mark of good scientists is that they go to great pains to distinguish between what they know and what they don’t know. 

It later turned out that the Lancet letter had been organized and drafted by Peter Daszak, ... This acute conflict of interest was not declared to the Lancet’s readers. To the contrary, the letter concluded, “We declare no competing interests.”

Wade points out that there is no direct evidence for either of the two hypotheses (which he calls theories).

He also talks quite a bit about "who is to blame" and claims that we need to know the answer as to which hypothesis is correct in order to know how to prevent the next pandemic. However, I disagree. Based on the evidence we already have we can conclude the following.

A. New deadly viruses can be zoonotic. The best way to reduce their likelihood is to close wet markets and reduce environmental destruction.

B. Even if SARS2 did not spread from the "gain of function" research in Wuhan it is completely plausible that it could have. Thus, given such risks that research should be stopped until a case is made that the possible benefits outweigh the risks and that it is done with much greater transparency and regulation than currently.

For balance I include an extract from Wikipedia

In May 2021, Wade published an article which advanced the claim that COVID-19 likely originated from a leak at the Wuhan Institute of Virology.^[12][13] Wade's article generated significant controversy,^[14] and has become one of the most-cited pieces in support of the lab leak hypothesis.^[15] This claim is at odds with the prevailing view among scientists that the virus most likely has a zoonotic origin.^{[16][17][18][19]} Some experts have supported taking the lab leak possibility seriously, while the majority consider it very unlikely, calling it "speculative and unsupported".^[20][21] Others noted the explosive and implausible nature of Wade's allegations about virologists conspiring to avoid blame for causing the pandemic,^[22] with Science-Based Medicine among those calling Wade's argument a conspiracy theory.^[23]

Another article worth reading (recommended by a commenter on this blog) is

Beijing’s useful idiots: Science journals have encouraged and enforced a false Covid narrative by Ian Birrell.

Emergent quasi-particles and gauge fields in quantum matter

Unfortunately, there is a paucity of good review articles that give gentle introductions to current research in condensed matter, both for beginning graduate students and for curious non-experts. Too many reviews are exhaustive, in both senses of the word! Contemporary Physics is a journal that aims to address this problem. I should look at it more often. In 2009, there was a nice 50th-anniversary issue, featuring some significant articles, with retrospective commentary. For example, there is a fascinating article about Snow Crystals by F.C. Franks.

My UQ colleague, Ben Powell recently submitted a nice review to the journal.

Emergent particles and gauge fields in quantum matter 

I give a pedagogical introduction to some of the many particles and gauge fields that can emerge in correlated matter. The standard model of materials is built on Landau's foundational principles: adiabatic continuity and spontaneous symmetry breaking. These ideas lead to quasiparticles that inherit their quantum numbers from fundamental particles, Nambu-Goldstone bosons, the Anderson-Higgs mechanism, and topological defects in order parameters. I then describe the modern discovery of physics beyond the standard model. Here, quantum correlations (entanglement) and topology play key roles in defining the properties of matter. This can lead to fractionalised quasiparticles that carry only a fraction of the quantum numbers that define fundamental particles. These particles can have exotic properties: for example Majorana fermions are their own antiparticles, anyons have exchange statistics that are neither bosonic nor fermionic, and magnetic monopoles do not occur in the vacuum. Gauge fields emerge naturally in the description of highly correlated matter and can lead to gauge bosons. Relationships to the standard model of particle physics are discussed.

 

The discipline of scientific writing

Writing a paper is hard work. Writing a paper that is clear, engaging, and accurate is even harder. After you have written a draft or are reading a draft of a colleague or co-author I think the following discipline is important and worthwhile.

Go through every sentence and ask, is this true? Is it precise and accurate?

Let me illustrate with a concrete example. Consider the following different claims.

The experiments of Jones et al. proved that GaAs quantum wires are Luttinger liquids.

Jones et al. interpreted their experimental results on GaAs quantum wires in terms of the framework of Luttinger liquid theory.

Jones et al. fit their experimental data for the temperature dependence of the resistivity of a GaAs quantum wire to a power law, such as predicted by Luttinger liquid theory.

Jones et al. showed that their experimental data was inconsistent with Fermi liquid theory, but consistent with Luttinger theory.

Hopefully, the differences between these claims are clear.

This discipline becomes even more important when reporting one's own research. For example, just replace ``Jones et al." in the sentences above with "We".

Unfortunately, the rush to publish in luxury journals has increased the tendency of authors to not exercise the appropriate restraint and discipline required by scientific integrity.

Mental health matters

My mental health this year has been up and down. It is not particularly clear why I have struggled at times, given the sources of stress were not particularly bad. Thankfully, now I am the best I have been all year. This may be because I have been quite proactive in taking action. First, there are the basics: adequate sleep, downtime, exercise, and diet. At one point I also cut out all caffeine and alcohol. I also went to the psychologist several times, did more mindfulness exercises, and increased my medication, in consultation with my doctor.

This experience underscores some of the complexities and associated poor understanding of both mental illness and healing. There are biomedical, psychological, social, and spiritual dimensions. There is a high causal density, just like in public policy. Why did I get worse? Why did I get better? As a patient, I don't want to do a series of clinical trials on myself and just change one variable, one after the other. It is better to attack the problem by doing a lot of things that are generally believed to help.

Several people have brought to my attention a series of recent articles in Nature about the mental health of Ph.D. students. These include the following.

Nature’s survey of more than 6,000 graduate students reveals the turbulent nature of doctoral research. 
This stimulated an Editorial,
The mental health of PhD researchers demands urgent attention 
``Anxiety and depression in graduate students is worsening. The health of the next generation of researchers needs systemic change to research cultures.''

Both articles are worth reading, but depressing.

On the one hand, I think it is wonderful Nature is publicising the issue. On the other hand, to me, it is a case of corporate well-washing: where companies pass off responsibility for a problem they have helped create onto their employees or customers. Universities do similar things. If I was asked to name a for-profit company that has a negative influence on ``research culture'' over the past two decades it would be Nature Publishing Group, hands down!

Chemistry finally joins the arxiv era

The physics arXiv started way back in 1991. Yet chemists strongly resisted following suit. Indeed if you posted a preprint on the arXiv American Chemical Society (ACS) journals would not publish it.
Eight years ago, Derek Lowe, asked Why Isn't There an arXiv for chemistry?

Well, finally ACS has succumbed and set up their own chemrxiv and announced that they will consider manuscripts that have been posted on the arXiv.

I thank Ben Powell for letting me know about the promising development.

Management lessons not learned from the discovery of graphene

Don't follow the pack!

I just read the Random Walk to Graphene, by Andre Geim. It is the lecture he gave when receiving the 2010 Nobel Prize in Physics. I should have read it long ago but was motivated to read it now because the following sentence features in Joseph Martin's "purloined letter'' argument about why condensed matter physics lacks status.

Graphene has literally been before our eyes and under our noses for many centuries but was never recognized for what it really is.

I learned some nice science from the lecture. Foremost, it is a great story of scientific creativity, perseverance, and serendipity. However, I want to mention a few things that highlight how the story strongly conflicts with most views about how science is currently "managed" and people operate.

Geim starts by recounting his Ph.D. and early postdoc years. His Ph.D papers were cited twice, by co-authors.

The subject was dead a decade before I even started my Ph.D. However, every cloud has its silver lining and what I uniquely learned from that experience was that I should never torture research students by offering them “zombie” projects.

Several years later he worked on a new topic as a staff scientist in Russia.

This experience taught me an important lesson that introducing a new experimental system is generally more rewarding than trying to find new phenomena within crowded areas.

He notes that when after a six-month visiting postdoc in Nottingham he entered the Western postdoc market with an h-index of 1!

When he was in the Netherlands as a young faculty member in a high magnetic field lab he began to experiment in creative directions leading to investigations of "magnetic water" and the iconic experiment of the levitating frog for which he received an Ig Nobel Prize.

we saw balls of levitating water (Fig. 1). This was awesome. It took little time to realize that the physics behind this phenomenon was good old diamagnetism. It took much longer to adjust my intuition to the fact that the feeble magnetic response of water ($\sim$${10}^{}$${}^{}$${}^{}$), that is billions of times weaker than that of iron, was sufficient to compensate the Earth’s gravity. Many colleagues, including those who worked with high magnetic fields all their lives, were flabbergasted, and some of them even argued that this was a hoax.... 

The levitation experience was both interesting and addictive. It taught me the important lesson that poking in directions far away from my immediate area of expertise could lead to interesting results, even if the initial ideas were extremely basic. This in turn influenced my research style, as I started making similar exploratory detours that somehow acquired the name “Friday night experiments.” The term is of course inaccurate. No serious work can be accomplished in just one night. It usually requires many months of lateral thinking and digging through irrelevant literature without any clear idea in sight. 

The story of the discovery of graphene using cellotape [Scotch tape, sticky tape] was more complicated, circuitous, and involved a lot more hard work than I realised.

There were two dozen or so [friday night] experiments over a period of approximately 15 years and, as expected, most of them failed miserably. But there were three hits, the levitation, gecko tape, and graphene. 

The story of the first publication is interesting. It took nine months to get the paper into Science.

First, we submitted the manuscript to Nature. It was rejected and, when further information requested by referees was added, rejected again. According to one referee, our report did “not constitute a sufficient scientific advance.” Science referees were more generous (or more knowledgeable?), and the presentation was better polished by that time. In hindsight, I should have saved the time and nerves by submitting to a second-tier journal, even though we all felt that the results were groundbreaking.

This is consistent with my belief that there is not a lot of correlation between great discoveries and publication in luxury journals.

So what should we learn from this story?
First, we should all be a little more adventurous and take some risks and explore new areas. Previously, I have argued successful researchers should move onto new hard problems. 
A lot of this relates to diminishing returns and opportunity costs.
Yet, unfortunately, there are now significant institutional and cultural pressures against this. However, I think senior faculty have a responsibility to buck these trends.

Second, funding agencies and university management really need to learn from this story of graphene. It really goes against metrics, KPIs, short term goals, making people "accountable" for extremely well-defined timetables and research outcomes, and forcing/hiring people to work on the latest hot topic.

Graphene is cool! And I am sure that there is a lot that remains to be discovered about graphene. However, I find it disturbing that so many people have flocked to the field. A few years ago I met a faculty member from Manchester and they said they were on the out because they were not working on graphene and there was a lot of pressure for people to be working on it.

There is another side to the story that I am not sure what to make of which has an Australian connection. When Alan Gilbert was vice-chancellor at the University of Melbourne he tried to build a parallel private for-profit institution, Melbourne University Private. This turned out to be a massive failure, wasting hundreds of millions of dollars. In 2004 Gilbert moved to Manchester as Vice Chancellor. Of course, his main goal was to lift Manchester in the global rankings.
The Wikipedia page about Gilbert states,

According to the university's strategic plan^[8] (largely a copy of his [Gilbert's] earlier and now abandoned Melbourne Agenda (2002)^[9]) the university aims to have five Nobel Laureates on its staff by 2015, at least two of whom will have full-time appointments, and three of which it is intended to secure by 2007. During Gilbert's tenure as vice chancellor, a Nobel Prize winner in economics, Joseph Stiglitz, was appointed the head of the Brooks World Poverty Institute at Manchester, and Sir John Sulston was appointed to a chair in the Faculty of Life Sciences. After Gilbert's death Andre Geimand Konstantin Novoselov, both of whom were appointed before Gilbert moved to Manchester, were awarded the Nobel Prize for Physics in 2010.

From the little I know about Gilbert it is very hard for me to see how he would have supported Geim's approach to doing science, particularly given that there were not well-defined immediate benefits to the corporate sector.

Publishing for Majority World academics

Tomorrow I am giving a talk about academic publishing for a group of faculty and Ph.D students from African universities. The challenges they face are formidable.
Here are my slides.
As always, it is important not to reinvent the wheel.
There are already some excellent resources and organisations. 
A particularly relevant organisation is AuthorAID which is related to inasp, and has an online course starting right now.

Publishing Scientific Papers in the Developing World is a helpful book, stemming from a 2010 conference.
Erik Thulstrup has a nice chapter "How should a Young Researcher Write and Publish a Good Research Paper?"

Square ice on graphene?

As I have written many times before, water is fascinating, a rich source of diverse and unusual phenomena, and an unfortunate source of spurious research reports.
Polywater is the classic example of the latter.
I find the physics particularly interesting because of the interplay of hydrogen bonding and quantum nuclear effects such as zero-point motion and tunneling.

There is a fascinating paper
Polymorphism of Water in Two Dimensions
Tanglaw Roman and Axel Groß

The paper was stimulated by a Nature paper that claimed to experimentally observe square ice inside graphene nanocapillaries. Such a square structure is in contrast to the hexagonal structure found in regular three-dimensional ice.
Subsequent, theoretical calculations claimed to support this observation of square ice.
Here the authors use DFT-based methods to calculate the relative energies of a range of two-dimensional structures for free-standing sheets of water (both single layer and bilayers) and for sheets bounded by two layers of graphene.

The figure below summarises the authors results for free-standing layers showing how the relative stability of the different water structures depends on the area density of water molecules [which varies the length and strength of the hydrogen bonds].

On the science side, there are several interesting questions arise.
How much do the results depend on the choice of DFT functional used [RPBE with dispersion corrections]?
Would inclusion of the nuclear zero-point energy modify the relative stability of some of the structures, as it does for the water hexamer?
Quantum nuclear effects are particularly important when the hydrogen bond length [distance between oxygen atoms] is about 2.4 Angstroms. [I am not quite sure what area density this corresponds to for the different structures].

On the sociology side, this paper is another example of a distressingly common progression:
1. A paper in a luxury journal reports an exotic and exciting new result.
2. More papers appear, some supporting and some raising questions about the result.
3. A very careful analysis reported in a solid professional journal shows the original claim was largely wrong. This paper attracts few citations because the community has moved on to the latest exciting new "discovery" reported in a luxury journal.

I thank Tanglaw Roman for helpful discussions about his paper.

Metrics and mental health

I never thought I would write a post linking the two issues in the title.

I have been working on my talk on mental health for the School of Maths and Physics colloquium on friday. Here is the current version of my slides. I welcome any comments.

In my preparation I have become aware of a few more resources. A recent issue of Nature includes several articles, including:

An Editorial, What to do to improve postgraduate mental health.
Four researchers write from their own experience, How to handle the dark days of depression.
There is also A collection of resources.

On the one hand, it is wonderful that Nature is highlighting the issue. On the other hand, it would be nice if they reflected how Nature Publishing Group might actually be part of the problem, as they mindlessly promote metrics and their journals. It is a case of corporate "well-washing."

The link between metrics and mental health is brought out in a report to the Higher Education Funding Council for England: The Metric Tide, Report of the Independent Review of the Role of Metrics in Research Assessment and Management, July 2015. The preface states:

Too often, poorly designed evaluation criteria are dominating minds, distorting behaviour and determining careers. At their worst, metrics can contribute to what Rowan Williams, the former Archbishop of Canterbury, calls a “new barbarity” in our universities. 

The tragic case of Stefan Grimm, whose suicide in September 2014 led Imperial College to launch a review of its use of performance metrics, is a jolting reminder that what’s at stake in these debates is more than just the design of effective management systems. 

Metrics hold real power: they are constitutive of values, identities and livelihoods. 

Good scientists will have published errata

A colleague was recently distressed to find a significant error in a paper he had just published. There was a sign error in one calculation which effects the application of the theory to a particular class of materials. The physics and mathematics are correct but not some of the conclusions of the paper. He and his co-authors have submitted an errata to the paper.

I tried to encourage my colleague that although this is disappointing it is just part of being a good scientist. I was reminded of an old post based on a paper, The Seven Sins in Academic Behavior in the Natural Sciences by Wilfred F. van Gunsteren.

One could even defend the proposition that a scientist with a sizeable publication record in science who has not published a single corrigendum is unlikely to be a good scientist. Either he or she has done such simple work that nothing could go wrong, or he or she has committed the fifth sin in science [neglect of errors found after publication.  

This is not an excuse for the sloppy work which is becoming more and more common in science due to the rush to publish the most surprising and spectacular results.
Results do need to be carefully checked and double checked.
But we have to face the fact that mistakes will happen... just like car crashes, burnt toast, stubbed toes, catching colds, ...  Precautions should be taken, but inevitably they will fail sometimes...
The amount of checking should be in proportion to the importance and the surprise of the results.

I think my most significant errors were several in my first paper on hydrogen bonding. I pointed out the errors on this blog and in the second paper I wrote on hydrogen bonding. There was a fortuitous cancellation of errors that meant the conclusions of the first paper were still valid. Arguably, I should also publish an errata on the first paper.

I also think it is important that in public all co-authors take joint responsibility for errors. In particular, it is quite dubious for senior co-authors to shift the blame to junior co-authors. Many senior people are only too happy to take credit. They also have to accept liability.

What do you think about the errata criteria for a good scientist?

I also welcome your own stories about erratum.

What makes a good theory or modelling paper?

There is an excellent editorial in the journal Langmuir
Writing Theory and Modeling Papers for Langmuir: The Good, the Bad, and the Ugly
Han Zuilhof, Shu-Hong Yu, David S. Sholl

The article is written in the context of a specific journal, that has a focus on surface and colloid chemistry, and predominantly experimental papers and readers.
The article is structured around the five questions below, that should actually be asked about any theory or computational paper.

Who is the intended audience?
Specifically, will the paper have an influence on the experimental community?

Are approximations and limitations clearly described? 

What physical insight is gained? 

Where does theory touch reality? 
Specifically, how does the work relate to experiment? Does it suggest new experiments to test the theory?

How can calculations be made reproducible? 

This is helpful advice and good for anyone to reflect on. On the other hand, this is so basic that the need for such an editorial reflects how bad science, and particularly computational modelling, has gotten. It is just too easy to download some software, run it for some complex chemical system that is fashionable, produce some pretty graphs, and write a paper....

Should we be concerned about irreproducible results in condensed matter physics?

The problem of the irreproducibility of many results in psychology and medical research is getting a lot of attention. There is even an Wikipedia page about the Replication Crisis. In the USA the National Academies have just launched a study of the problem.

This naturally raises the question about how big is the problem is in physics and chemistry?

One survey showed that many chemists and physicists could not reproduce results of others. 

My anecdotal experience, is that for both experiments and computer simulations, there is a serious problem. Colleagues will often tell me privately they cannot reproduce the published results of others. Furthermore, this particularly seems to be a problem for "high impact" results, published in luxury journals. A concrete example is the case of USO's [Unidentified Superconducting Objects]. Here is just one specific case.

A recent paper looks at the problem for the case of a basic measurement in a very popular class of materials.

How Reproducible Are Isotherm Measurements in Metal–Organic Frameworks? 
 Jongwoo Park, Joshua D. Howe, and David S. Sholl

We show that for the well-studied case of CO2 adsorption there are only 15 of the thousands of known MOFs for which enough experiments have been reported to allow strong conclusions to be drawn about the reproducibility of these measurements.

Unlike most university press releases [which are too often full of misleading hype] the one from Georgia Tech associated with this paper is actually quite informative and worth reading.

A paper worth reading is that by John Ioannidis, "Why most published research findings are false", as it contains some nice basic statistical arguments as to why people should be publishing null results. He also makes the provocative statement:

The hotter a scientific field (with more scientific teams involved) the less likely the research findings are to be true.

I thank Sheri Kim and David Sholl for stimulating this post.

How serious do you think this problem is? What are the best ways to address the problem?

Refereeing papers: recent experiences at the coal face

I am not a big fan of the peer review process. Too often it is a superficial ritual that adds little scientific value. Nevertheless, when it does work I think it can be very valuable. Here are some of my recent experiences that I thought were rather positive, and may be marginally interesting to readers.

I was sent a paper by JCP to review. Overall, I liked it but I thought it would benefit from some significant revisions. In a weird coincidence, I was visiting the same institution as some of the authors. I have been recently challenged about whether peer review really should be anonymous [see this discussion of SciPost] and so I took a risk. I signed my report and sent a copy to all the authors and told them I would be happy to meet to discuss the paper. We met and had a nice discussion. However, it was interesting that JCP told me that they had deleted my self-identification as it was against their policy.

I was sent a paper by PRL to review that I (and other referees) took a strong dislike to. The cover letter was also "Interesting". I wrote a concrete critical report. However, for the first time ever, I used the box for "Comments that will only be seen by the Editors". I said the authors had inappropriately used and cited my own work, that the paper was in the class "Not even wrong", and that if PRL published it, PRLs reputation in a certain community would suffer. Maybe I am a coward, but I am glad I was anonymous.

I got a paper I liked to review from JCP. However, the authors did not engage with a whole physics literature that was relevant to the paper and they needed to use it to sharpen their results. I think the final paper will be much better and more interesting.

A recent paper with my postdoc got two critical but constructive reports from PRB. This required some new calculations and comparisons but was much better as a result. Today we heard it was accepted.

I now decline all referee requests from luxury journals. I have limited time and would prefer to invest in journals that I think are making a positive contribution to science.

Have you had any recent positive experiences as a referee or received a helpful report?

Important distinctions in the debate about journals

My post, "Do we need more journals?" generated a lot of comments, showing that the associated issues are something people have strong opinions about.

I think it important to consider some distinct questions that the community needs to debate.

What research fields, topics, and projects should we work on?

When is a specific research result worth communicating to the relevant research community?

Who should be co-authors of that communication?

What is the best method of communicating that result to the community?

How should the "performance" and "potential" of individuals, departments, and institutions be evaluated?

A major problem for science is that over the past two decades the dominant answer to the last question (metrics such as Journal "Impact" Factors and citations) is determining the answer to the other questions. This issue has been nicely discussed by Carl Caves.
The tail is wagging the dog.

People flock to "hot" topics that can produce quick papers, may attract a lot of citations, and are beloved by the editors of luxury journals. Results are often obtained and analysed in a rush, not checked adequately, and presented in the "best" possible light with a bias towards exotic explanations. Co-authors are sometimes determined by career issues and the prospect of increasing the probability of publication in a luxury journal, rather than by scientific contribution.

Finally, there is a meta-question that is in the background. The question is actually more important but harder to answer.
How are the answers to the last question being driven by broader moral and political issues?
Examples include the rise of the neoliberal management class, treatment of employees, democracy in the workplace, inequality, post-truth, the value of status and "success", economic instrumentalism, ...

Do we really need more journals?

NO!

Nature Publishing Group continues to spawn "Baby Natures" like crazy.

I was disappointed to see that Physical Review is launching a new journal Physical Review Materials. They claim it is to better serve the materials community. I found this strange. What is wrong with Physical Review B? It does a great job.
Surely, the real reason is APS wants to compete with Nature Materials [a front for mediocrity and hype] which has a big Journal Impact Factor (JIF).
On the other hand, if the new journal could put Nature Materials out of business I would be very happy. At least the journal would be run and controlled by real scientists and not-for-profit.

So I just want to rant two points I have made before.

First, the JIF is essentially meaningless, particularly when it comes to evaluating the quality of individual papers. Even if one believes citations are some sort of useful measure of impact, one should look at the distribution, not just the mean. Below the distribution is shown for Nature Chemistry.

Note how the distribution is highly skewed, being dominated by a few highly cited papers. More than 70 per cent of papers score less than the mean.

Second, the problem is that people are publishing too many papers. We need less journals not more!
Three years ago, I posted about how I think journals are actually redundant and gave a specific proposal of how to move towards a system that produces better science (more efficiently) and more accurately evaluates the quality of individuals contributions.

Getting there will obviously be difficult. However, initiatives such as SciPost and PLOS ONE, are steps in a positive direction.
Meanwhile those of us evaluating the "performance" of individuals can focus on real science and not all this nonsense beloved by many.

Should you put "theory" or "experiment" in the title of your paper?

A referee for a recent paper, entitled "Effect of hydrogen bonding on infrared absorption intensity", suggested that we should add "theory" to the title since the chosen title could equally be about an experimental paper. In the end, we declined but did make the abstract clearer that the paper was purely theoretical.

I thought this is an interesting issue, that I had not thought about explicitly before. If you look at titles of papers it is true that it is sometimes not clear whether the paper is theoretical, experimental, or joint theory and experiment. This is particularly true with theory papers with titles such as "Property X of material ABC" or experimental papers with titles such as "Strong electron correlations in materials class Y". To experts who working are on the same topic or who know the authors it may be obvious. But to others, it may not be so obvious.

Does it matter?
Surely if the abstract makes it clear then it is o.k.?
[Again it is amazing how for some abstracts in luxury journals you have to read to practically the last sentence to figure it out. This is because experimental papers can be clothed in theoretical hype].

The suggestion prompted me to do two things.
First, I looked through the titles of most of my papers and found that the only ones which contained "theory" were those which referred to a particular technique, e.g. "Dynamical mean-field theory" or "linear spin wave theory".

Second, I looked at the titles of some famous papers, such as BCS and by P.W. Anderson.
BCS is "Theory of superconductivity" and the abstract begins "A theory...".
PWA does have "theory" in some papers but not others.

The only conclusion I came to from all of this is that I think we should work hard on the titles (and abstracts) of our papers, since the title may determine whether or not they are read.

Maybe it is tangential, but it also reminded me that like Anderson, I am largely against combined theory and experiment papers.

What do you think? Does it matter?