Last week I organized a workshop on the future of academic publication. My point was that our current system, based on private pre-publication peer review, is archaic. I noted that the way the peer review system is currently organized (where external reviewers judge both the quality of the science and the interest for the journal) represents just a few decades in the history of science. It can hardly qualify as the way science is or should be done. It is a historical feature. For example, only one of Einstein’s papers was formally peer-reviewed; Crick & Watson’s DNA paper was not formally peer-reviewed. Many journals introduced external peer review in the 1960s or 1970s to deal with the growth in the number and variety of submissions (see e.g. Baldwin, 2015); before that, editors would decide whether to publish the papers they received, depending on the number of pages they could print.
Given the possibilities that offers the internet, it seems that there is no reason anymore to couple the two current roles of peer review: editorial selection and scientific discussion. One could simply share their work online, get feedback from the community to discuss the work, and then let people recommend papers to their colleagues and compile all sorts of reader’s digests. No time wasted in multiple submissions, no prestige misattributed to publications in glamour journals, who do not do a better a job than any other journal at pointing errors and frauds. Just the science and the public discussion of science.
But there is a lot of resistance to this idea, namely the idea that papers should be formally approved by peer reviewers before they are published. Because otherwise, so many people claim, the scientific world would be polluted by all sorts of unverified claims. It would not be science anymore, just gossip. I have attributed this attitude to conservatism, first because as noted above this system is a rather recent addition to the scientific enterprise, and second because papers are published before peer review. We call those “preprints”, but really these are scientific papers made public, so by definition they are published. I follow the preprints in my field and I don’t see any particular loss in quality.
However, I think I was missing a key element. The more profound reason why many people, in particular experimental biologists, are so attached to peer review is in my view that they hold naive philosophical views about the notion of truth in science. A paper should be peer-reviewed because otherwise you can’t cite it as a true fact. Peer review validates science, thanks to experts who make sure that the claims of the authors are actually true. Of course it can go wrong and reviewers might miss something, but it is the purpose of peer review. This view is reflected in the tendency, especially in biology journals, to choose titles that look like established truths: “Hunger is controlled by HGRase”, instead of “The molecular control of hunger”. Scientists and journalists can then write revealed truths with a verse reference, such as “Hunger is controlled by HGRase (McDonald et al., 2017)”.
The great misunderstanding is that truth is a notion that applies to logical propositions (for example, mathematical theorems), not to empirical claims. This has been well argued by Popper, for example. Truth is by nature a theoretical concept. Everything said is said with words, and in this sense it always refers to theoretical concepts. One can only judge whether observations are congruent with the meaning attributed to the words, and that meaning necessarily has a theoretical nature. There is no such thing as an “established fact”. This is so even of what we might consider as direct observations. Take for example the claim “The resting potential of neurons is -70 mV”. This is a theoretical statement. Why? First, because to establish it, I have recorded a number of neurons. If you test it, it will be on a different neuron, which I have not measured. So I am making a theoretical claim. Probably, I also tested my neurons with a particular method (not mentioning a particular region and species). But my claim makes no reference to the method by which I have made the inference. That would be the “methods” part of my paper, not the conclusion, and when you cite my paper, you will cite it because of the conclusion, the “established fact”, you will not be referring to the methods, which you consider are the means to establish the fact. It is the role of the reviewers to check the methods, to check that they do establish the fact.
But these are trivial remarks. It is not just that the method matters. The very notion of an observation always implicitly relies on a theoretical background. When I say that the resting potential is -70 mV, I mean that there is a potential difference of -70 mV across the membrane. But that’s not what I measure. I measure the difference in potential between some point outside the cell and the inside of a patch pipette whose solution is in contact with the cell’s inside. So I am assuming the potential is the same in all points of the cytosol, even though I have not tested it. I am also implicitly modeling the cytosol as a solution, even though the reality is more complex than that, given the mass of charged proteins in it. I am assuming that the extracellular potential is constant. I am assuming that my pipette solution reasonably matches the actual cytosol solution, given that “solution” is only a convenient model. I am implicitly making all sorts of theoretical assumptions, which have a lot of empirical support but are still of a theoretical nature.
I have tried with this example to show that even a very simple “fact” is actually a theoretical proposition, with many layers of assumptions. But of course in general, papers typically make claims that rely less firmly on accepted theoretical grounds, since they must be “novel”. So it is never the case that a paper definitely proves its conclusions. Because conclusions have a theoretical nature, all that can be checked is whether observations are consistent with the authors’ interpretation.
So the goal of peer review can’t be to establish the truth. If it were the case, then why would reviewers ever disagree? They disagree because they cannot actually judge whether a claim is true; they can only say whether they are personally convinced. This makes the current peer review system extremely poor, because all the information we get is: two anonymous people were convinced (and maybe others were not, but we’ll never find out). What would be more useful would be to have an open public discussion, with criticisms, qualifications and alternative interpretations fully disclosed for anyone to read and make their own opinion. In such a system, the notion of a stamp of approval on a paper would simply be absurd; why hide the disapprovals? There is the paper, and there is the scientific discussion of the paper, and that is all there needs to be.
There is some concern these days that peer reviewed research is unreliable. Well, science is unreliable. That is almost what defines it: it can be criticized and revised. Seeing peer review as the system that establishes the scientific truth is not only a historical error, it is a great philosophical error, and a dangerous bureaucratic view of science. We don’t need editorial decisions based on peer review. We need free publication (we have it) and we need open scientific discussion (it’s coming). That’s all we need.