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Thank you for the revised manuscript which sucessfully addressed the reviewer's comments.
While most of reviewers' comments were successfully addressed in the revised manuscript, one of the reviewers still has important comments about the evidence-base for the conclusions of the article. Also, I would advise that you clearly address possible differences in research fields or practices of large collaborative groups in assigning authorship and "producing" prolific authors (although you did not have such cases in your samples).
No comments.
No comments.
Despite the rebuttal (and minor changes to the text/tables), the conclusions and suggestions, in my opinion, are not based on presented evidence.
The evidence only shows that there are authors who publish a lot. A tiny fraction of all researchers who we know next to nothing about to be able to substantiate the assumptions from the manuscript (P2, lines 29-32 and P2, lines 35-37).
I have reread the entire manuscript and the rebuttals several times and still do not find that the Discussion and the final conclusions are based on evidence.
The data do seem to point to a possible problem in authorship policies "enforced" by the journals the investigated authors have been publishing in. But even so, the entire population of extremely "productive" researchers boil down to less than 1% of the overall investigated publications/author.
The two cases of fraud are the only, if anecdotal, evidence that it is possible to perform research misconduct while also being a scribe-maniac. But that is the benefit of hindsight.
One cannot expect institutions to police journal authorship policies. Or to enforce a different set of rules on highly productive authors.
At least not based on the presented evidence.
The answers of the authors to referees' comments look reasonable. I think the revised version is acceptable for publication.
The answers of the authors to referees' comments look reasonable. I think the revised version is acceptable for publication.
The answers of the authors to referees' comments look reasonable. I think the revised version is acceptable for publication.
The answers of the authors to referees' comments look reasonable. I think the revised version is acceptable for publication.
Dear Liz,
We have now received comments from three reviewers and all of them have important questions about your study. Please pay special attention to the comments of the reviewer No. 1, who questions the problem of prolific authors in large collaboratiive projects.
(see validity/general comments)
(see validity/general comments)
Although I appreciate the underlying idea and motivation, I'm afraid that this study belongs to the early 20th century, or perhaps even the 19th century, when researchers were indeed mostly working closed in their own labs/homes and publishing single-author studies (or books, actually). Yes, if someone in the 19th century published 100 books in a single year, I would find that suspicious. I could be critical about this study, but I simply can't, because I genuinely feel surprised that - 15 years into the 21st century - the authors can be entirely oblivious to all the key progress that information technology, "big data" science, opportunities for communication, biobanks and high-throughput methods, social media and so many other wonders of technology did to accelerate science. The cutting edge of science in nearly all areas today - from genomics to epigenomics, bioinformatics, intervention trials, particle physics, astronomy, social sciences and even econometrics - belongs to massive international collaborations, such as those exhibited in human genome project (HGP) or large hadron collider (LHC). No-one I know who works in the "cutting edge" in any area of science cares about the "authorship" in the sense the authors still seem to perceive it. Today, we're all happy to contribute to these massive projects in order to overcome the limitations that plagued science throughout its history and led to endless cases of false-positive results due to poorly designed, small studies in individual labs - which were far more damaging to science than a few extreme cases of fraud which the authors mention (and which were detected much more easily, and dealt with, that the enormous body of false-positive reports that is far more difficult to deal with). Because of this, I don't find most of the content of the paper valid in the 21st century context.
Today, scientists are increasingly happy to give up their individual recognition in order to be able to contribute to a truly important research, answering truly big questions - they only care about "contributorship", and not about the "authorship". As an example, after many hundreds of people were involved in conceptualising the human genome project, getting funding (3 billion US$ in the 1980s!), working for 11 years in 14 labs around the world to read every single letter, then put it all together in the computers and perform endless checks, the paper reporting on the project could have been written by a clever medical writer in 3 weeks. Does that mean that this writer should have been the only author and that he/she should get all the prizes? Of course not. Massively collaborative research leads to highly efficient distribution of tasks, which also include preparation of papers. The KEY difference between highly productive scientists who deserve their contribution mentioned, and those that are suspicious, will be in their average citations per paper. If the authors publish many papers, and all those papers are cited more than those of other authors, the likely explanation is their involvement in massively collaborative, big data projects, which result in better science. This isn't really "authorship", it's "contributorship", and it is nearly always well-deserved, in my own experience. However, if someone publishes many papers but the average citation per paper is very low, it's a likely sign of a "salami-publisher", "duplicate-publisher", "free ride publisher", or another fraud-like behaviour. I think these two situations need to be very clearly distinguished. In conclusion, I think that the paper is outdated. I envisage that, in the coming years, there will be researchers whose contribution will (deservingly!) be mentioned on hundreds of papers within a single year, on which they will be listed together with hundreds, or perhaps thousands of their colleagues. These papers will originate from large international consortia, and they will report much better, and more interesting, science than the average oligo-authored paper. I see absolutely nothing wrong with this and I am actually very much looking forward to it.
The manuscript adheres to all PeerJ policies.
While this is a snapshot view of a limited number of highly productive authors, it is unclear what the hypothesis of the research was, as the ideas put forward in the Introduction have not been tested/substantiated by the analysis.
The methods are clear enough the be reproducible although too much emphasis has been put on (automatic) elimination of (sur)name-sakes. The end effect is a hugely reduced database that describes only a small subset of 4 discreet topics.
Also, the authors claim to have manually analyzed the 10 most prolific authors for each topic, yet in Table 2. they describe a total of 10 most prolific authors, further reducing the view of the whole.
The data are limited, as they pool from a large database but analyze only a fraction of the whole. This then influences the conclusions one can draw from the data.
While interesting, the results are discussed poorly and the conclusions of the need to warn the institutions/funders of possibly excessive authorship are not substantiated.
The rest of the conclusions are too general/generic and fall within the categories of the responsible conduct of research in general.
The anecdotal "evidence" of increased fraud in extremely productive authors has not been confirmed or discussed. Neither has the assumption of guest authorship been analyzed/confirmed/discussed.
I suggest the authors reanalyze the data, but set a limit for the number and type of publications per year/per 5-year period that they define as "excessive", as even in the most prolific authors (analyzed), the number of research articles vs. total published articles was below 20% (if, as the authors present their data, the clinical trials are not counted as "research"). Therefore, I suggest the authors do not limit the analysis to just the 4 discreet topics, but to the number of published articles, especially the ones that (most likely) influence the decision making of the possible funders/employers.
While I am not saying that authorship on published (multi-author) clinical trials, or case reports, reviews, and editorials should be trivialized, the hypothesis of increased likelihood of fraud in excessive authorship may be more concerned with research articles (as the authors of the manuscript detail on the case of J.H. Schon's publication record). Y. Fujii's publications of fabricated clinical trials, in my mind, also belong to the "research" articles group.
The authors may want to discuss the high portion of "middle" positions on the byline, as a possible guest/gift authorship practice. Again, as far as I know, the funding agencies and institutions do not necessarily reward/hire "middle" authorships, but rather prefer the "doers" (first on the byline) and the "enablers" (last on the byline).
All in all, this is a worthy topic of investigation, but more data and a greater level of analysis is needed to be able to make the described "intuitive" and "anecdotal" conclusions.
In this manuscript the authors present the results of their study on authorship pattern of prolific authors between 2008 and 2012. Using a bespoke software, they searched MEDLINE to collect the necessary data and found that less than 1% of authors published a substantially high number of articles in the study period and that many of which can be attributed to gift authorship. They concluded that institutions and bodies responsible for career promotion should treat these prolific authors with more caution.
The English as well as the Introduction, and the structure is fine.
The design is not described in enough detail to be reproducible. It needs more elaboration:
1) Is there any reason the authors choose to study the four topics of epilepsy, RA, renal and liver transplantation?
2) As the software used in this study is at the heart of methodology, the authors need to elaborate more about its details. In the way the authors describe this bespoke software, the study is not reproducible at all.
1) The statement “unfeasibly large” is not a well-defined scientific/scientometrics term. The authors should either define the term or avoid its use.
2) Is there any reason the authors choose to study the four topics of epilepsy, RA, renal and liver transplantation?
3) As the software used in this study is at the heart of methodology, the authors need to elaborate more about its details. In the way the authors describe this bespoke software, the study is not reproducible at all.
4) For presentation of data, instead of presenting the median and range (lines 60, 61), it is better to provide the median and interquartile range (IQR); IQR is a better measure for dispersion than the range.
5) In line 75, the numbers in parentheses are better to be preceded by “n=”; then, instead of “Germany (6)”, we’ll have “Germany (n=6)”.
6) There are miscalculations in Table 2: For example for Author 2, summing up the number of authors in the 1st, middle, and last positions is 137 NOT 138 (as it is mentioned under the Total column). The same is also true for Author 3 (140 authors based on positions vs 138 under Total column)! Such miscalculations make us become suspicious about the software used, which has not been tested rigorously.
7) In the Discussion and Conclusion section, the authors are better to focus on the main issue of the manuscript rather than describing or commenting on how the identities of the authors can be ascertained (say through use of ORCID, etc in lines 95-97). We expect the authors describe why such distribution is probably seen? Why most of these prolific authors occupy the Middle positions? Is there any difference in the number of authors of articles these prolific authors coauthored compared to other articles published in the same field? Are most of these prolific authors chairs of their departments, influential persons, etc, so that they can receive gift authorship?
8) References 2 and 7 cite URLs; we need to mention when the Web page was visited. Furthermore, citing the homepage of ICMJE is not enough; please be specific as possible. The homepage does not provide the information the authors addressing. Perhaps a better URL would be http://www.icmje.org/recommendations/browse/roles-and-responsibilities/defining-the-role-of-authors-and-contributors.html
1) The statement “unfeasibly large” is not a well-defined scientific/scientometrics term. The authors should either define the term or avoid its use.
2) Is there any reason the authors choose to study the four topics of epilepsy, RA, renal and liver transplantation?
3) As the software used in this study is at the heart of methodology, the authors need to elaborate more about its details. In the way the authors describe this bespoke software, the study is not reproducible at all.
4) For presentation of data, instead of presenting the median and range (lines 60, 61), it is better to provide the median and interquartile range (IQR); IQR is a better measure for dispersion than the range.
5) In line 75, the numbers in parentheses are better to be preceded by “n=”; then, instead of “Germany (6)”, we’ll have “Germany (n=6)”.
6) There are miscalculations in Table 2: For example for Author 2, summing up the number of authors in the 1st, middle, and last positions is 137 NOT 138 (as it is mentioned under the Total column). The same is also true for Author 3 (140 authors based on positions vs 138 under Total column)! Such miscalculations make us become suspicious about the software used, which has not been tested rigorously.
7) In the Discussion and Conclusion section, the authors are better to focus on the main issue of the manuscript rather than describing or commenting on how the identities of the authors can be ascertained (say through use of ORCID, etc in lines 95-97). We expect the authors describe why such distribution is probably seen? Why most of these prolific authors occupy the Middle positions? Is there any difference in the number of authors of articles these prolific authors coauthored compared to other articles published in the same field? Are most of these prolific authors chairs of their departments, influential persons, etc, so that they can receive gift authorship?
8) References 2 and 7 cite URLs; we need to mention when the Web page was visited. Furthermore, citing the homepage of ICMJE is not enough; please be specific as possible. The homepage does not provide the information the authors addressing. Perhaps a better URL would be http://www.icmje.org/recommendations/browse/roles-and-responsibilities/defining-the-role-of-authors-and-contributors.html
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