Papers that triumphed over their rejections

The imperfections of peer-review and editorial judgements are widely acknowledged; most of us know of very significant foundational scientific results that were rejected by the major journals and magazines but have nonetheless stood the test of time and proven of exceptional importance to science. The goal of this posting (work in progress) is to compile a list of such papers. I have limited the list below only to papers that proved to be exceptionally influential and for which there are traceable written accounts of their rejections. Although the discoveries described by most of these rejected papers have been awarded the Nobel Prize, this has not been a criterion in compiling this list nor will it be as I expand it. Suggestions are most welcomed!

The weak interaction (beta decay), 1933

Fermi, E (1934). An attempt of a theory of beta radiation. Z. phys, 88(161), 10.

Nature Editors: It contained speculations too remote from reality to be of interest to the reader

[Rajasekaran, 2014, page 20], Wikipedia

The Krebs cycle, 1937

Krebs, H, Johnson, WA (1937) The role of citric acid in intermediate metabolism in animal tissues. Enzymologia, 4, 148-156.

Hans Krebs: The paper was returned [from Nature] to me five days later accompanied by a letter of rejection written in the formal style of those days. This was the first time in my career, after having published more than fifty papers, that I had rejection or semi-rejection

[Krebs, 1981, page 98]
A year before Enzymologia published Kreb’s work, Nature published a welcome for Enzymologia that is remarkably relevant to our current concerns!

FT NMR, 1966

Ernst, RR, Anderson WA (1966) Application of Fourier transform spectroscopy to magnetic resonance. Review of Scientific Instruments, 37, 93-102.

Richard Ernst: The paper that described our achievements [awarded the 1991 Nobel Prize in Chemistry] was rejected twice by the Journal of Chemical Physics to be finally accepted and published in the Review of Scientific Instruments.

[Ernst, 1991]

The Cell Division Cycle, 1974

Hartwell LH, Culotti J, Pringle JR, Reid BJ (1974) Genetic control of the cell division cycle in yeast. Science 183:46–51.

John Pringle: Hartwell et al. (1974) was rejected without review by Nature, leaving a bad taste that has lasted…

[Pringle, 2013]

PCR, 1987

Mullis, KB, Faloona, FA (1987) Specific synthesis of DNA in vitro via a polymerase-catalyzed chain reaction, Methods in Enzymology, 155, 335-350.

Kary Mullis: I knew PCR would spread across the world like wild fire. This time there was no doubt in my mind: Nature would publish it. They rejected it. So did Science …  Fuck them, I said

[Mullis, 1998, page 105]

References

Ernst R. (1991) Biographical, http://www.nobelprize.org/

Krebs, H. (1981), Reminiscences and Reflections, Clarendon Press, Oxford.

Mullis, K. (1998), Dancing Naked in the Mind Field, Vintage Books, New York

Pringle, J. R. (2013). An enduring enthusiasm for academic science, but with concerns. Molecular biology of the cell, 24(21), 3281-3284.

Rajasekaran, G. (2014). Fermi and the theory of weak interactions.Resonance, 19(1), 18-44.

The Best Projects Are Least Obvious

We are fortunate to live in an exciting time. Today, new technologies enable the design and execution of straightforward experiments, many of which were not possible just a few years ago. These experiments hold the potential to bring new discoveries and to improve medical care. An abundance of obvious-next-step experiments creates a buzz of activities and excitement that is quite palpable among graduate students, postdocs, and professors alike.

Such enthusiasm permeates the air and stimulates; it also overwhelms. It seems there is always so much to do and never enough time to do it. Recent findings have opened up many new research avenues, and emerging technologies are ever-alluring. How are investigators to pursue all of these things, given our limited time? Or, failing that, how can we at least choose the best leads to follow?

Much of the aforementioned buzz is often the result of an overabundance of next-step projects that are obvious to most researchers. Many of these projects are quite good, but rarely are they exceptional — at least in the sense that they result in a nontrivial connection. It’s not often that these projects help researchers advance their fields. Many such projects use novel, fashionable technologies, but bring little new perspective to the scientific community. Yet I have seen colleagues become so busy pursuing such experiments that they lack the time to complete most of their projects, or to even think conceptually and creatively.

Of course, some next-step experiments are poised to become major landmarks, as were the first gene expression measurement by RNA-seq, the first comprehensive mass spectroscopy-based quantification of a eukaryotic proteome, the first gene deletion collection, the first analysis of conserved DNA sequences in mammalian genomes, and the first induction of pluripotent stem cells. If I do not pursue the obvious experiments likely to become landmarks, someone else will, and science will progress without delay. These tempting experiments typically lure multiple independent groups, at least some of which abandon the projects once their competitors’ first big paper has been published.

Thus, none of the many tempting next-step experiments — even among these that are poised to be landmarks — is likely the best to do if I want to make a difference. After all, the many experiments that are obvious to me are likely to be obvious to most of my colleagues. Few of the most tempting experiments are likely to bring genuinely new perspectives to standing problems or find new important problems. In fact, I find that the more obvious an experiment is to me, the less likely it is to evoke a new perspective, no matter what new and fashionable technologies are used. What’s more, the more tied up I become with next-step experiments, the less time I have to think of truly great ones.

The overabundance of stimulating next-step experiments contrasts strikingly with a dearth of genuinely new perspectives. Focusing on the genuinely creative ideas rephrases the original question of “How can I possibly follow all of the many tempting avenues?” to a harder, but potentially much more fruitful question: “How can I chart a course that is truly worth following?”

An edited version of this opinion essay was published by The Scientist: The Best Projects Are Least Obvious