Science paper genres

First a caveat: there is a literature on how science works. GG doesn’t delve into that literature, so some of this may be nonsense. But it is nonsense of a scientist and this leads in an odd direction. You’ve been warned…

This might surprise some folks (probably not many who read this blog), but not all science papers (or “articles”) are the same. There are four distinct types of science papers in GG’s zoo, and it can be helpful to be aware of this as you encounter them. [OK, missed a fifth caught by a commenter…so exercise to the reader is to fit it in].

The most common paper is the one you envision from high school science, the paper where some data was gathered and analyzed and shared. These papers are the building blocks of science; call them brick papers. They are rarely the highly cited papers, instead contributing another brick in the massive edifice of science.

Another relatively common paper is the overview paper. These tend to congregate in specific journals with “review” in their name as well as various book volumes where the contribution is anticipated to be more long lived in usage. These can be really difficult to assemble and write (the Decade of North American Geology, or DNAG, volumes of the late 1980s are a prime example). These attempt to pull together all those individual bricks together. The result is some combination of creating a bigger picture and identifying points of controversy. Such papers don’t generally solve any conflicts, instead typically falling back on “more research is needed.” These papers are often very highly cited as they allow a later researcher to plop in a citation to a review paper instead of a mind-numbing list of 20 or 30 papers that might be relevant (and might be worth citing so that potential reviewers aren’t feeling left out). These can help guide the science going forward.

A related genre are synthesis papers. You might think these are simple overview papers, but in a way these are to overview papers as editorials are to news reporting. There is a slant there that the author(s) pursue. Conflicting observations are shot down, supporting evidence is propped up, and a distinct conclusion is reached. These too can be widely cited if their chief conclusion proves to be popular. Or, sometimes, they are highly cited as a strawman quickly demolished in later papers in pursuit of completeness. In either case, how they deal with conflicting evidence can clearly identify the strongest points to be reexamined.

Finally there are papers that propose a different view of the field altogether. Call them alternative view papers, or maybe dissenting papers. Some will emerge from a rich literature review, so in a sense a synthesis paper; others emerge from a small set of observations, typically of a new type, but what they share is an expansion of viewpoints to include a perspective absent from the literature to that point. J. Tuzo Wilson’s 1965 paper on transform faults is an excellent example (indeed, many early plate tectonics papers land in this category). Although these usually emerge from some dissatisfaction with existing theory, they are far enough from the mainstream that both points of support and objection are utterly different and so open new lines of research.

You can kind of follow the progress of science through the kinds of papers being published on some broad topic. You almost always are starting from brick papers (it is hard to do otherwise). At some point there are efforts to pull together the bricks as something more coherent; call it grasping for a theory. This will first emerge in an overview paper or possibly a synthesis paper. It is then refined by repeated beatings in both some brick papers specifically aimed to test ideas and in synthesis papers that seek to prune and shape the theory to better fit observations. After awhile, they return the thesis, now polished, to the overview papers where the thesis is reaffirmed.

At this point two things can happen. One is that the core theory is reaffirmed with minimal contortions and becomes the root of other theories. The other is that trouble starts to emerge. Some of the brick papers produce observations that aren’t fitting the theory well. As these pile up, synthesis papers seek to adjust the theory; overview papers satisfy themselves to point out where the problems are. At some point dissenting papers emerge, throwing out different or even wildly different ideas. These set up totally new avenues for synthesis papers, namely to test some new theory against the old.

You can find this thread in many corners of earth science. An obvious one is the evolution and eventual demise of geosynclinal theory. Emerging from the early observations of the Appalachians, this theory flourished as the basic observations of thickening of strata into mountain belts piled up. But as fossil discrepancies emerged and adjoining geologies were occasionally utterly incompatible, synthesis papers struggled to introduce adjustments to geosynclinal theory to address these challenges. While Wegener’s continental drift peeled off some geologists (mainly in Europe), it really was the mobilist view from plate tectonics, coming from the new observations of the seafloor, that produced a suite of dissenting papers that reinterpreted the geology of geosynclines to show that geology was easily fit into moving plates.

A more compact example might be the uplift of the Sierra Nevada. By the 1970s geologists felt confident that the range had risen over the past 5-10 million years, largely based on the notion that erosion = uplift. That truism took hits from a couple of papers around 1990. Freed from that straitjacket, a dissenting paper exploited a new approach using low-temperature geochronology, offering a very different take on the Sierra, arguing that its elevation was in fact quite old. This opened the door to a number of new studies, some supporting the old range, others defending the young range, a debate that continues today.

OK, so what? Well, GG was pondering his own publication record and realized he liked to try to write the dissenting paper. This started with a Tectonics paper arguing that a thinner than accepted Sierra crust was consistent with a young range, then a Geosphere paper offering up a “hydrodynamic” means of driving the Laramide orogeny instead of a flat slab coupled to North America, and more recently a Geology paper adding alteration of the crust from fluids to proposals for creating the High Plains. This continues as GG wrestles with a paper looking to question the subduction of an oceanic plateau in creating the geology of the Mojave Desert region (as many posts here document). Here’s the thing: the Tectonics paper was from thesis work, so essentially unsupposed by a dedicated grant. The Geosphere paper was really a grant proposal, so when visualized and drafted, it was unsupported by a grant. The Geology paper similarly lacked support, and this Mojave paper has certainly been a pro bono effort. Why? Well, how do you write a proposal that says “I am going to revisit and possibly overturn current hypotheses simply by pulling up all the existing literature and digesting it”? The answer is, you can’t (well, maybe you can; GG hasn’t had luck there). You have to do that spadework first. Hence the Tectonics paper led to a field deployment supported by an endowed postdoc; the Geosphere paper led to a grant that funded some new work on the Laramide. The Geology paper continues to provide motivation for funded work by GG’s colleagues on evidence for hydration of the crust during the Laramide.

The point? These dissenting papers–papers that advocate for a different viewpoint–are not ones supported by our current grant machinery (despite the appearance of grant numbers in the acknowledgements). Grantsmanship revolves around brick papers (and not even overview or synthesis papers). What is the hypothesis, how will the gathered data bear on the hypothesis, dot i’s and cross t’s to get dollars. NSF wants to fund transformative science, but you can’t propose it until you have figured it out, and just where is that supposed to happen?

GG once argued that we have support all backwards. Getting grants is really hard while frankly you can get almost anything published if you are dedicated enough. So GG suggested you pay for results: you get payment for papers. This would make peer review a lot better motivated, and freedom from reviewing the avalanche of grant proposals should open up some time for thorough paper reviews. Maybe you do this in an odd way (instead of a pile of $100 bills, have access to an account upon which you can draw for scientific needs; instead of “reject” or “accept” reviewers suggest cash amounts), but those are details. In essence, if you demonstrate ability, we hand over money and you decide how to go forward. If it is a synthesis that is needed to really get a bead on a problem, spend your chits on doing that. If it is field work, off you go without two or three rounds of perfecting the the timeline while the student who really fits the project graduates and moves on.

Whatever. We need the brick papers, there is no doubt. But we need these other papers, too, and we aren’t doing a very good job of getting them made. This arguably makes intellectual ruts deeper than necessary and so consideration of alternate views a tougher sell than simply on the merits. So maybe like mid-20th century U.S. geologists, we cling to an old conceptualization well beyond its expiration date.