One reason I blog: no peer review

Science ain’t easy. I know being a marine biologist must sound really glamorous but it is 90% email and less than 1% swimming with dolphins (or seahorses in Helen’s case).

Case in point: peer review. Here’s how it works: (1) submit manuscript to a journal, (2) wait a few months, (3) get a rejection email from the editor along with 2-3 mean-spirited rarely constructive evaluations of your work from your peers, (4) repeat at a new journal (luckily there are many of them). Fun Huh!

Example; this good news email I just got from an editor (who is a friend, colleague and a fellow-surfer!) at the new ESA journal Ecosphere:

Dear Dr. Bruno:

Thank you very much for submitting your manuscript “Coral reef baselines: how much macroalgae is natural?” for review by Ecosphere. Based on the second review, we will not be able to accept this manuscript for publication in the journal.

I’m sorry that the news was not better from the second reviewer. Their initial concerns were clearly stated, but your revision was clearly not enough to satisfy them. I think the issue of macro algae is something we could have worked around, but the reviewer’s call for a more analytical treatment is a fair one, and one that may not be possible at this point, given the limited data. As sometimes happens, the second review is even stronger in its objections, an indication of a frustrated reviewer. The reviewer’s comments are very well thought out, though no doubt you will disagree with some of them. In such cases, I have to defer to the reviewer who has a far greater in-depth knowledge of the subject than I do.

The reviews are attached, and we hope they will help you should you decide to revise the manuscript for submission elsewhere. Thank you again for thinking of the Journals of the Ecological Society. We will look forward to further contributions from you and your colleagues.

Sincerely,

Kevin Lafferty
Subject-matter Editor
Ecosphere

This was the second review at Ecosphere. Maybe I am biased, but Reviewer #1 seems to have a bit of a chip on his shoulder, e.g., his suggestion that we publish the manuscript in the “blog-o-sphere” rather than in a scientific journal (see his full reviews below). Good thing I have a website!

Seriously, this is what passes for objective and careful peer review at journals of the Ecological Society of America. Note: (1) I am also an ESA editor, (2) this manuscript was also rejected at FEE, another ESA journal (a far worse experience that I will blog about soon…), (3) Ecosphere is a brand new journal that I was invited to be the editor of! Not that my decision to pass on that offer affected my reviews, but it goes to show, everyone gets treated equally badly in peer review. Finally, no, I don’t know who Reviewer #1 is: peer review is usually anonymous. If it weren’t do you think people would behave so poorly?

PS; you can read the guidelines for Ecosphere reviewers here

Reviewer #1 (First review)

Other Journal(s): blog-o-sphere

The manuscript by Bruno and colleagues provides an ecological thought piece regarding the distribution of ‘macroalgae’ on coral reefs. The authors use a collection of information from the literature to consider what should be termed as the baseline state of coral reef benthic communities, focusing solely on the cover of one suite of algae. Three sets of data are used to explore patterns of macroalgal cover on reefs: (1) a few surveys of reefs on two Caribbean islands in the 1970s, (2) summaries of data from islands of the remote Pacific, and (3) summarized data from surveys conducted from 1996-2006 used from an earlier publication of the first author. Comparing historical data (from 1) to quasi-pristine reefs (from 2), the authors note that macroalgal cover was lower in the Caribbean than in the Pacific. Further, comparing each the historical data and the data from quasi-pristine reefs to the summarized data (from 3), they show that many modern reefs have less macroalgae than these putative baselines. The authors use this information to provide various suggestions for the academic and management community.

Importantly, this paper can only be reviewed as an idea paper. There are no new data or analyses presented, and the review of the literature is scattered and far from comprehensive. Although this is not necessarily bad (in fact, I enjoy reading people’s opinions on topics, though maybe not in scientific journals…), there are some important gaps reasoning that prevent me from being positive about this ms.

1) Simplistic definition of ‘macroalgae’ – The authors state their definition of ‘macroalgae’ as “large, anatomically complex algal forms including erect calcifying species but not filamentous algae, i.e., turfs.” By using this definition, it is really difficult to interpret the findings of the comparisons. For example, calcified erect macroalgae are ecologically quite different from fleshy erect macroalgae. Definitions of ‘nuisance’ macroalgae most frequently include just the fleshy species, and transitions of algal assemblages from more calcifying to more fleshy can occur with no changes in total cover of ‘macroalgae’. Further, there is concern with omitting reference to turf algae in considerations of perceived negative impacts of ‘macroalgae’ (and let’s not forget that turfs actually are proper macroalgae from a phycological perspective!). Many of the negative effects attributed to macroalgae in this manuscript are also caused by turf algae, e.g. reducing coral recruit survival and inhibiting adult coral growth. Further, the turf algae are probably the most preferred of the algal types by herbivorous fishes, so any consideration of total foraging impacts on algae has to consider the role of turf algae. Without a clearer and more precise definition of the algal types, these musings about growth, succession, and herbivory are extremely limited.

2) Discussion of trophic cascades – The authors spend a lot of time working through a thought exercise regarding the role of trophic cascades in mediating changes in the cover of macroalgae. First off, it will be essentially impossible to treat this topic without including data from the entire functional group of readily consumable algae, and this would have to include algal turfs (see above). Further, the musings on trophic cascades in this paper are largely devoid of data or even references to relevant studies. I know of no evidence linking predators in a 3-level trophic pathway through to algae on a coral reef. The reason, I would believe, is due to the high complexity within functional levels on coral reefs. A good review of the evidence for trophic cascades across ecosystems is in a recent book edited by Terborgh and Estes, and includes a chapter by Sandin and colleagues specifically on coral reefs. Without any evidence from coral reefs functionally linking predators throughherbivores to algae, we are left with only musings. Further, models of top-down control are not the only ‘lessons from theoretical ecology’, and countless other models might be more relevant. It would be much more powerful to reinforce this thought piece with some true modeling with the assumptions formalized and justified.

Without providing any new data, significant analyses, or comprehensive synthesis, this paper does not seem fitting for the primary literature. Instead, it seems a more conversational (and at time combative) piece based largely on opinion. I encourage the authors to re-consider their motivation for this manuscript and re-draft to a more appropriate venue or with more scientifically appropriate content.

Our responses (in red) to Reviewer #1’s first review:

Other Journal(s): blog-o-sphere

Does Ecosphere count as the “blog-o-sphere”?  🙂

Importantly, this paper can only be reviewed as an idea paper. There are no new data or analyses presented, and the review of the literature is scattered and far from comprehensive. Although this is not necessarily bad (in fact, I enjoy reading people’s opinions on topics, though maybe not in scientific journals…), there are some important gaps reasoning that prevent me from being positive about this ms.

There may be no new data, however, there are new ideas and new data syntheses.

1) Simplistic definition of ‘macroalgae’ – The authors state their definition of ‘macroalgae’ as “large, anatomically complex algal forms including erect calcifying species but not filamentous algae, i.e., turfs.” By using this definition, it is really difficult to interpret the findings of the comparisons. For example, calcified erect macroalgae are ecologically quite different from fleshy erect macroalgae.

See above and lines 56-76 in the revised manuscript.  We agree there are obviously many ecological differences among the subgroups that constitute “macroalgae” but in the context of this paper, we feel using this very, very widely used functional group is necessary and justifiable.  Lumping taxa together to communicate ideas in ecology is common and unavoidable.  Indeed, this reviewer lumps diverse groups including turf algae, herbivorous fish and predators.  Functional groups like “plants” and even “herbaceous plants” obviously contain very diverse taxa yet are commonplace in the ecological literature.  What is important is to justify the grouping and functional group usage, which we have now done in the Introduction.

Definitions of ‘nuisance’ macroalgae most frequently include just the fleshy species,

True for some systems, particularly estuaries.  The only coral reef scientists that use the term “nuisance algae” are indeed working on eutrophication and responses by a few fleshy taxa like Enteromorpha (eg, Lapointe).  When coral reef scientists consider algae thought to negatively affect juvenile corals, they use the “macroalgae” functional group.

and transitions of algal assemblages from more calcifying to more fleshy can occur with no changes in total cover of ‘macroalgae’.

True in theory, yet this isn’t documented to our knowledge and changes in the revise direction are just as likely.  But we are not talking about such compositional shifts in this paper, although we agree, they would be interesting to look at.

Further, there is concern with omitting reference to turf algae in considerations of perceived negative impacts of ‘macroalgae’ (and let’s not forget that turfs actually are proper macroalgae from a phycological perspective!). Many of the negative effects attributed to macroalgae in this manuscript are also caused by turf algae, e.g. reducing coral recruit survival and inhibiting adult coral growth.

Possibly. Unfortunately, there is so little work on turfs in this context, we really don’t know what role they are playing, how this has changed, etc.

Further, the turf algae are probably the most preferred of the algal types by herbivorous fishes,

Regardless of what they “prefer”, herbivorous fishes and inverts clearly eat macroalgae and have strong effects on macroalgal biomass and cover as has been shown by countless experiments and large-scale survey work.

Further, the musings on trophic cascades in this paper are largely devoid of data or even references to relevant studies. I know of no evidence linking predators in a 3-level trophic pathway through to algae on a coral reef.

We cited several relevant studies including Madin et al 2010 (on which the editor played an important role).

Further, models of top-down control are not the only ‘lessons from theoretical ecology’, and countless other models might be more relevant. It would be much more powerful to reinforce this thought piece with some true modeling with the assumptions formalized and justified.

We have cut the “lessons from theoretical ecology” subheading.  Original coral reef modeling is well outside of the scope of this paper.

Reviewer #1 (second review; meant to be Reviewer #1’s response to our response):

The revised manuscript by Bruno and colleagues posits that one current definition of a management target for coral reef ecosystems is not well substantiated. The authors focus their discussion on the definition of a ‘baseline’ for macroalgal cover on coral reefs. The authors link the definition of a baseline with a management target. The authors make the case that the low accuracy and precision of macroalgal baselines requires that we not adopt a single target value in discussions with reef managers. As argued in the ms, the low accuracy is a product of poorly designed studies and cascading trophic events that have not been considered. The low precision is due to implicit variability of oceanography, geography, and history across space and time. The brief introduction to the limits of data precision regarding algal community composition is the strongest portion of this manuscript.

A valuable contribution to the literature would be a rigorous academic treatment of these issues of accuracy and precision, including a comprehensive review of the literature and/or detailed analysis of relevant data. This manuscript falls far short of this goal. Arguments are developed based on very limited reference to the relevant literature, and the style is less academic and more combative. For many points, one quotation is proffered to substantiate a claim of widespread acceptance of the point throughout the literature. This one-sidedness introduces important biases that limit the value of this ms as an academic review. For other points, the authors are clear to cite the lack of consensus in the literature (e.g., uncertainty regarding historic densities of sea urchins in the Caribbean and undecided relative importance of nutrient vs herbivore control of seaweed), leaving the logical argument of the discussion point particularly incomplete. Is the debate unfounded, with the
balance of evidence favoring one point? Or does the crux of the debate rely on the implicit variability of nature? The references to the literature, instead, read as academic cherry-picking, where the claim was made first and a reference was found to substantiate. As a review paper, a fair and equitable reading of the literature is prerequisite. And if the authors have a logical counter-argument for findings that are not in alignment with their claim, it is critical to explain the reasoning.

Beyond style, I find the definition of “macroalgae” used in this ms to remain troublesome. In Line 58, the authors state that they will use macroalgal cover as a key indicator of reef state, following “broad consensus of coral reef scientists”. The foundation for this consensus, as presented, is one quotation. There are actually a number of indicators that are regularly used to describe reef state, with coral cover probably the most pervasive. In the field, when coral cover is lost, then some other benthic type will overtake the liberated space. The authors are keying in on the indication that some discussion in the literature has stated that macroalgae can fill this void. Importantly, “macroalgae” as space-fillers include a broad spectrum of fleshy and erect calcifying algae, including turf algae. The authors take pains to justify why they do not treat turf algae in this manuscript, but none of the rationale is biological. Instead, the focus is on just a subset of algal taxa, as
they state is disproportionately reported in the literature. I find this focus on an incomplete metric of algal community composition to be counter-productive toward the advancement of meaningful science, and again largely combative. Much more justification is needed to motivate this dedication to a limited definition of macroalgae. Better yet, the authors could offer some insights for advancing the field with an improved vision/definition of benthic “health”, with specific reference to seaweeds.

Finally, I fear that this manuscript chases a red herring with reference to management. The authors set as their goal to refute the promotion of invariant management targets in units of “macroalgal cover” (with the definition of macroalgae a point of ecological concern). No examples of such targets are presented in the ms, and I cannot think of any that are being applied. The most analogous target is the establishment of management protocols specifically protecting herbivorous fishes. As I read this ms, I do not believe that the authors would argue against the importance of such a management goal. So the stated management relevance of this ms seems misguided. Only by maintaining critical members of the reef community, namely the herbivores, can we hope to maintain, using the words of these authors, baseline distributions on coral reefs. If the primary goal of this ms is to reach managers, I fear that the authors will only lead to confusion and, worse yet, the delay of protections
for important reef players like herbivores. As drafted, this ms suggests that a “key indicator” of reef health, macroalgal cover, likely is not too different from historical levels (see my concerns with this summary, above). Without more rigor in terminology, this ms could lead the management community to conclude that herbivore protection is not important. If the authors do believe that the introduction of new management measures protecting herbivores is misguided, I recommend stating this directly (and again justifying the reasoning). This would be much clearer. Instead, if the abandonment of herbivore (and other fishery) management protocols is not the goal, please think carefully about the argument that is being drafted. I would hate the authors to realize unintended consequences if the abandonment of hard-fought management action was not their design.

Other specific comments:

Title – Fix the grammar. The word “macroalgae” is plural.

Line 108 – The comments about the historical importance of macroalgae pulled from the Brawley and Adey paper are misleading. The cited paper discusses damselfish territories in and among intact thickets of Acropora cervicornis. Thus, these seaweeds are a secondary part of the benthic community, capitalizing on the indirect sunlight that gets through the live coral tips. The sunlight arriving to these seaweeds is reduced, as the corals have ‘won’ the competition for direct sunlight. If the authors are debating the importance of this seaweed in these indirect positions, they will need to generate a new metric of cover. Typically, we use ‘cover’ to mean the percentage of benthos occupied when viewed from directly above. This is a good approximation of the major light incidence. Using this metric, seaweed will be only a minor benthic constituent within branching coral thickets. As such, this discussion of the importance of seaweeds is off-topical to the thesis of the paper that cover
of seaweed is or is not a reliable indicator of reef health. Further, as damselfish affect cover largely of turf algae, this discussion reinforces the problem with excluding turfs from the definition of “macroalgae”.

Line 113 – Citing unpublished data as a strong counterpoint to published results without explanation of the data set itself is not appropriate. Was this one transect or 100? Without any explanation of the methods and effort, the numbers are meaningless to the reader.

Line 273 and thereabouts – The discussion of trophic cascades remains elementary. For example, the Madin et al ms cites the potential importance of behavioral modifications, but fails to taken into account changes in relative abundances of species across predator gradients. If the density shifts of herbivores are profound enough, the behavioral modifications will be moot. The theory of trophic cascades is not as straightforward as the authors portray (i.e., with more predators there is necessarily less herbivory). Without more dedicated treatment of the topic, the text reads as naïve. For example, the strong assertion (including the use of italics) beginning on Line 296 is in no way substantiated in this ms, let alone in the suite of empirical research that is not cited here.

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