Tag: publishing

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Show us the data now damnit! Excuses are running out.

A very interesting paper from Caroline Savage and Andrew Vickers was published in PLoS ONE last week detailing an empirical study of data sharing of PLoS journal authors. The results themselves, that one out ten corresponding authors provided data, are not particularly surprising, mirroring as they do previous studies, both formal [pdf] and informal (also from Vickers, I assume this is a different data set), of data sharing.

Nor are the reasons why data was not shared particularly new. Two authors couldn’t be tracked down at all. Several did not reply and the remainder came up with the usual excuses; “too hard”, “need more information”, “university policy forbids it”. The numbers in the study are small and it is a shame it wasn’t possible to do a wider study that might have teased out discipline, gender, and age differences in attitude. Such a study really ought to be done but it isn’t clear to me how to do it effectively, properly, or indeed ethically. The reason why small numbers were chosen was both to focus on PLoS authors, who might be expected to have more open attitudes, and to make the request from the authors, that the data was to be used in a Master educational project, plausible.

So while helpful, the paper itself isn’t doesn’t provide much that is new. What will be interesting will be to see how PLoS responds. These authors are clearly violating stated PLoS policy on data sharing (see e.g. PLoS ONE policy). The papers should arguably be publicly pulled from the journals. Most journals have similar policies on data sharing, and most have no corporate interest in actually enforcing them. I am unaware of any cases where a paper has been retracted due to the authors unwillingness to share (if there are examples I’d love to know about them! [Ed. Hilary Spencer from NPG pointed us in the direction of some case studies in a presentation from Philip Campbell).

Is it fair that a small group be used as a scapegoat? Is it really necessary to go for the nuclear option and pull the papers? As was said in a Friendfeed discussion thread on the paper: “IME [In my experience] researchers are reeeeeeeally good at calling bluffs. I think there’s no other way“. I can’t see any other way of raising the profile of this issue. Should PLoS take the risk of being seen as hardline on this? Risking the consequences of people not sending papers there because of the need to reveal data?

The PLoS offering has always been about quality, high profile journals delivering important papers, and at PLoS ONE critical analysis of the quality of the methodology. The perceived value of that quality is compromised by authors who do not make data available. My personal view is that PLoS would win by taking a hard line and the moral high ground. Your paper might be important enough to get into Journal X, but is the data of sufficient quality to make it into PLoS ONE? Other journals would be forced to follow – at least those that take quality seriously.

There will always be cases where data can not or should not be available. But these should be carefully delineated exceptions and not the rule. If you can’t be bothered putting your data into a shape worthy of publication then the conclusions you have based on that data are worthless. You should not be allowed to publish. End of. We are running out of excuses. The time to make the data available is now. If it isn’t backed by the data then it shouldn’t be published.

Update: It is clear from this editorial blog post from the PLoS Medicine editors that PLoS do not in fact know which papers are involved.  As was pointed out by Steve Koch in the friendfeed discussion there is an irony that Savage and Vickers have not, in a sense, provided their own raw data i.e. the emails and names of correspondents. However I would accept that to do so would be a an unethical breach of presumed privacy as the correspondents might reasonably have expected these were private emails and to publish names would effectively be entrapment. Life is never straightforward and this is precisely the kind of grey area we need more explicit guidance on.

Savage CJ, Vickers AJ (2009) Empirical Study of Data Sharing by Authors Publishing in PLoS Journals. PLoS ONE 4(9): e7078. doi:10.1371/journal.pone.0007078

Full disclosure: I am an academic editor for PLoS ONE and have raised the issue of insisting on supporting data for all charts and graphs in PLoS ONE papers in the editors’ forum. There is also a recent paper with my name on in which the words “data not shown” appear. If anyone wants that data I will make sure they get it, and as soon as Nature enable article commenting we’ll try to get something up there. The usual excuses apply, and don’t really cut the mustard.

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Some (probably not original) thoughts about originality

A number of things have prompted me to be thinking about what makes a piece of writing “original” in a web based world where we might draft things in the open, get informal public peer review, where un-refereed conference posters can be published online, and pre-print servers of submitted versions of papers are increasingly widely used. I’m in the process of correcting an invited paper that derives mostly from a set of blog posts and had to revise another piece because it was too much like a blog post but what got me thinking most was a discussion on the PLoS ONE Academic Editors forum about the originality requirements for PLoS ONE.

In particular the question arose of papers that have been previously peer reviewed and published, but in journals that are not indexed or that very few people have access to. Many of us have one or two papers in journals that are essentially inaccessible, local society journals or just journals that were never online, and never widely enough distributed for anyone to find. I have a paper in Complex Systems (volume 17, issue 4 since you ask) that is not indexed in Pubmed, only available in a preprint archive and has effectively no citations. Probably because it isn’t in an index and no-one has ever found it.  But it describes a nice piece of work that we went through hell to publish because we hoped someone might find it useful.

Now everyone agreed, and this is what the PLoS ONE submission policy says quite clearly, that such a paper cannot be submitted for publication. This is essentially a restatement of the Ingelfinger Rule. But being the contrary person I am I started wondering why. For a commercial publisher with a subscripton business model it is clear that you don’t want to take on content that you can’t exert a copyright over, but for a non-profit with a mission to bring science to wider audience does this really make sense? If the science is currently unaccessible and is of appropriate quality for a given journal and the authors are willing to pay the costs to bring it to a wider public, why is this not allowed?

The reason usually given is that if something is “already published” then we don’t need another version. But if something is effectively inaccessible is that not true. Are preprints, conference proceedings, even privately circulated copies, not “already published”. There is also still a strong sense that there needs to be a “version of record”, that there is a potential for confusion with different versions. There is a need for better practice in the citation of different versions of work but this is a problem we already have. Again a version in an obscure place is unlikely to cause confusion. Another reason is that refereeing is a scarce resource that needs to be protected. This points to our failure to publish and re-use referee’s reports within the current system, to actually realise the value that we (claim to) ascribe to them. But again, if the author is willing to pay for this, why should they not be allowed to?

However, in my view, at the core to the rejection of “republication” is an objection to the idea that people might manage to get double credit for a single publication. In a world where the numbers matter people do game the system to maximise the number of papers they have. Credit where credit’s due is a good principle and people feel, rightly, uneasy with people getting more credit for the same work published in the same form. I think there are three answers to this, one social, one technical, and one…well lets just call it heretical.

Firstly placing two versions of a manuscript on the same CV is simply bad practice. Physicists don’t list both the ArXiv and journal versions of papers on their publication lists. In most disciplines, where conference papers are not peer reviewed, they are listed separate to formally published peer reviewed papers in CVs. We have strong social norms around “double counting”. These differ from discipline to discipline as to whether work presented at conferences can be published as a journal paper, whether pre-prints are widely accepted, and how control needs to be exerted over media releases but while there may be differences over what constitutes “the same paper” there are storng social norms that you only publish the same thing once.  These social norms are at the root of the objection to re-publication.

Secondly the technical identification of duplicate available versions, either deliberately by the authors to avoid potential confusion, or in an investigative roleto identify potential misconduct, is now trivial. A quick search can rapidly identify duplicate versions of papers. I note paranthetically that it would be even easier with a fully open access corpus but where there is either misconduct, or the potential for confusion, tools like Turnitin and Google will sort it out for you pretty quickly.

Finally though, for me the strongest answer to the concern over “double credit” is that this is a deep indication we have the whole issue backwards. Are we really more concerned about someone having an extra paper on their CV than we are about getting the science into the hands of as many people as possible? This seems to me a strong indication that we value the role of the paper as a virtual notch on the bedpost over its role in communicating results. We should never forget that STM publishing is a multibillion dollar industry supported primarily through public subsidy. There are cheaper ways to provide people with CV points if that is all we care about.

This is a place where the author (or funder) pays model really comes it in its own. If an author feels strongly enough that a paper will get to a wider audience in a new journal, if they feel strongly enough that it will benefit from that journal’s peer review process, and they are prepared to pay a fee for that publication, why should they be prevented from doing so? If that publication does bring that science to a wider audience, is not a public service publisher discharging their mission through that publication?

Now I’m not going to recommend this as a change in policy to PLoS. It’s far too radical and would probably raise more problems in terms of public relations than it would solve in terms of science communication. But I do want to question the motivations that lie at the bottom of this traditional prohibition. As I have said before and will probably say over and over (and over) again. We are spending public money here. We need to be clear about what it is we are buying, whether it is primarily for career measurement or communication, and whether we are getting the best possible value for money. If we don’t ask the question, then in my view we don’t deserve the funding.

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The Future of the Paper…does it have one? (and the answer is yes!)

A session entitled “The Future of the Paper” at Science Online London 2009 was a panel made up of an interesting set of people, Lee-Ann Coleman from the British Library, Katharine Barnes the editor of Nature Protocols, Theo Bloom from PLoS and Enrico Balli of SISSA Medialab.

The panelists rehearsed many of the issues and problems that have been discussed before and I won’t re-hash here. My feeling was that the panelists didn’t offer a radical enough view of the possibilities but there was an interesting discussion around what a paper was for and where it was going. My own thinking on this has been recently revolving around the importance of a narrative as a human route into the data. It might be argued that if the whole scientific enterprise could be made machine readable then we wouldn’t need papers. Lee-Ann argued and I agree that the paper as the human readable version will retain an important place. Our scientific model building exploits our particular skill as story tellers, something computers remain extremely poor at.

But this is becoming an increasingly smaller part of the overall record itself. For a growing band of scientists the paper is only a means of citing a dataset or an idea. We need to widen the idea of what the literature is and what it is made up of. To do this we need to make all of these objects stable and citeable. As Phil Lord pointed out this isn’t enough because you also have to make those objects and their citations “count” for career credit. My personal view is that the market in talent will actually drive the adoption of wider metrics that are essentially variations of Page Rank because other metrics will become increasingly useless, and the market will become increasingly efficient as geographical location becomes gradually less important. But I’m almost certainly over optimistic about how effective this will be.

Where I thought the panel didn’t go far enough was in questioning the form of the paper as an object within a journal. Essentially each presentation became “and because there wasn’t a journal for this kind of thing we created/will create a new one”. To me the problem isn’t the paper. As I said above the idea of a narrative document is a useful and important one. The problem is that we keep thinking in terms of journals, as though a pair of covers around a set of paper documents has any relevance in the modern world.

The journal used to play an important role in publication. The publisher still has an important role but we need to step outside the notion of the journal and present different types of content and objects in the best way for that set of objects. The journal as brand may still have a role to play although I think that is increasingly going to be important only at the very top of the market. The idea of the journal is both constraining our thinking about how best to publish different types of research object and distorting the way we do and communicate science. Data publication should be optimized for access to and discoverability of data, software publication should make the software available and useable. Neither are particularly helped by putting “papers” in “journals”. They are helped by creating stable, appropriate publication mechanisms, with appropriate review mechanisms, making them citeable and making them valued. The point at which our response to needing to publish things stops being “well we’d better create a journal for that” then we might just have made it into the 21st century.

But the paper remains the way we tell story’s about and around our science. And if us dumb humans are going to keep doing science then it will continue to be an important part of the way we go about that.

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Some slides for granting permissions (or not) in presentations

A couple of weeks ago there was a significant fracas over Daniel MacArthur‘s tweeting from a Cold Spring Harbour Laboratory meeting.  This was followed in pretty quick succession by an article in Nature discussing the problems that could be caused when the details of presentations no longer stop at the walls of the conference room and all of these led to a discussion (see also friendfeed discussions) about how to make it clear whether you are happy or not with your presentation being photographed, videoed, or live blogged. A couple of suggestions were made for logos or icons that might be used.

I thought it might be helpful rather than a single logo to have a panel that allows the presenter to permit some activities but not others and put together a couple of mockups.

Permission to do whatever with presentationPermission to do less with presentation

I’ve also uploaded a PowerPoint file with the two of these as slides to Slideshare which should enable you to download, modify, and extract the images as you wish. In both cases they are listed as having CC-BY licences but feel free to use them without any attribution to me.

In some of the Friendfeed conversations there are some good comments about how best to represent and suggestions on possible improvements. In particular Anders Norgaard suggests a slightly more friendly “please don’t” rather than my “do not”. Entirely up to you, but I just wanted to get these out. At the moment these are really just to prompt discussion but if you find them useful then please re-post modified versions for others to use.

[Ed. The social media icons are from Chris Ross and are by default under a GPL license. I have a request in to make them available to the Public Domain or as CC-BY at least for re-use. And yes I should have picked this up before.]

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Google Wave in Research – the slightly more sober view – Part I – Papers

I, and many others have spent the last week thinking about Wave and I have to say that I am getting more, rather than less, excited about the possibilities that this represents. All of the below will have to remain speculation for the moment but I wanted to walk through two use cases and identify how the concept of a collaborative automated document will have an impact. In this post I will start with the drafting and publication of a paper because it is an easier step to think about. In the next post I will move on to the use of Wave as a laboratory recording tool.

Drafting and publishing a paper via Wave

I start drafting the text of a new paper. As I do this I add the Creative Commons robot as a participant. The robot will ask what license I wish to use and then provide a stamp, linked back to the license terms. When a new participant adds text or material to the document, they will be asked whether they are happy with the license, and their agreement will be registered within a private blip within the Wave controlled by the Robot (probably called CC-bly, pronounced see-see-bly). The robot may also register the document with a central repository of open content. A second robot could notify the authors respective institutional repository, creating a negative click repository in, well one click. More seriously this would allow the IR to track, and if appropriate modify, the document as well as harvest its content and metadata automatically.

I invite a series of authors to contribute to the paper and we start to write. Naturally the inline commenting and collaborative authoring tools get a good workout and it is possible to watch the evolution of specific sections with the playback tool. The authors are geographically distributed but we can organize scheduled hacking sessions with inline chat to work on sections of the paper. As we start to add references the Reference Formatter gets added (not sure whether this is a Robot or an Gadget, but it is almost certainly called “Reffy”). The formatter automatically recognizes text of the form (Smythe and Hoofback 1876) and searches the Citeulike libraries of the authors for the appropriate reference, adds an inline citation, and places a formatted reference in a separate Wavelet to keep it protected from random edits. Chunks of text can be collected from reports or theses in other Waves and the tracking system notes where they have come from, maintaing the history of the whole document and its sources and checking licenses for compatibility. Terminology checkers can be run over the document, based on the existing Spelly extension (although at the moment this works on the internal not the external API – Google say they are working to fix that) that check for incorrect or ambiguous use of terms, or identify gene names, structures etc. and automatically format them and link them to the reference database.

It is time to add some data and charts to the paper. The actual source data are held in an online spreadsheet. A chart/graphing widget is added to the document and formats the data into a default graph which the user can then modify as they wish. The link back to the live data is of course maintained. Ideally this will trigger the CC-bly robot to query the user as to whether they wish to dedicate the data to the Public Domain (therefore satisfying both the Science Commons Data protocol and the Open Knowledge Definition – see how smoothly I got that in?). When the users says yes (being a right thinking person) the data is marked with the chosen waiver/dedication and CKAN is notified and a record created of the new dataset.

The paper is cleaned up – informal comments can be easily obtained by adding colleagues to the Wave. Submission is as simple as adding a new participant, the journal robot (PLoSsy obviously) to the Wave. The journal is running its own Wave server so referees can be given anonymous accounts on that system if they choose. Review can happen directly within the document with a conversation between authors, reviewers, and editors. You don’t need to wait for some system to aggregate a set of comments and send them in one hit and you can deal with issues directly in conversation with the people who raise them. In addition the contribution of editors and referees to the final document is explicitly tracked. Because the journal runs its own server, not only can the referees and editors have private conversations that the authors don’t see, those conversations need never leave the journal server and are as secure as they can reasonably be expected to be.

Once accepted the paper is published simply by adding a new participant. What would traditionally happen at this point is that a completely new typeset version would be created, breaking the link with everything that has gone before. This could be done by creating a new Wave with just the finalized version visible and all comments stripped out. What would be far more exciting would be for a formatted version to be created which retained the entire history. A major objection to publishing referees comments is that they refer to the unpublished version. Here the reader can see the comments in context and come to their own conclusions. Before publishing any inline data will need to be harvested and placed in a reliable repository along with any other additional information. Supplementary information can simple be hidden under “folds” within the document rather than buried in separate documents.

The published document is then a living thing. The canonical “as published” version is clearly marked but the functionality for comments or updates or complete revisions is built in. The modular XML nature of the Wave means that there is a natural means of citing a specific portion of the document. In the future citations to a specific point in a paper could be marked, again via a widget or robot, to provide a back link to the citing source. Harvesters can traverse this graph of links in both directions easily wiring up the published data graph.

Based on the currently published information none of the above is even particularly difficult to implement. Much of it will require some careful study of how the work flows operate in practice and there will likely be issues of collisions and complications but most of the above is simply based on the functionality demonstrated at the Wave launch. The real challenge will lie in integration with existing publishing and document management systems and with the subtle social implications that changing the way that authors, referees, editors, and readers interact with the document. Should readers be allowed to comment directly in the Wave or should that be in a separate Wavelet? Will referees want to be anonymous and will authors be happy to see the history made public?

Much will depend on how reliable and how responsive the technology really is, as well as how easy it is to build the functionality described above. But the bottom line is that this is the result of about four day’s occasional idle thinking about what can be done. When we really start building and realizing what we can do, that is when the revolution will start.

Part II is here.

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A breakthrough on data licensing for public science?

I spent two days this week visiting Peter Murray-Rust and others at the Unilever Centre for Molecular Informatics at Cambridge. There was a lot of useful discussion and I learned an awful lot that requires more thinking and will no doubt result in further posts. In this one I want to relay a conversation we had over lunch with Peter, Jim Downing, Nico Adams, Nick Day and Rufus Pollock that seemed extremely productive. It should be noted that what follows is my recollection so may not be entirely accurate and shouldn’t be taken to accurately represent other people’s views necessarily.

The appropriate way to license published scientific data is an argument that has now been rolling on for some time. Broadly speaking the argument has devolved into two camps. Firstly those who have a belief in the value of share-alike or copyleft provisions of GPL and similar licenses. Many of these people come from an Open Source Software or Open Content background. The primary concern of this group is spreading the message and use of Open Content and to prevent “freeloaders” from being able to use Open material and not contribute back to the open community. A presumption in this view is that a license is a good, or at least acceptable, way of achieving both these goals. Also included here are those who think that it is important to allow people the freedom to address their concerns through copyleft approaches. I think it is fair to characterize Rufus as falling into this latter group.

On the other side are those, including myself, who are concerned more centrally with enabling re-use and re-purposing of data as far as is possible. Most of us are scientists of one sort or another and not programmers per se. We don’t tend to be concerned about freeloading (or in some cases welcome it as effective re-use). Another common characteristic is that we have been prevented from being able to make our own content as free as we would like due to copyleft provisions. I prefer to make all my content CC-BY (or cc0 where possible). I am frequently limited in my ability to do this by the wish to incorporate CC-BY-SA or GFDL material. We are deeply worried by the potential for licensing to make it harder to re-use and re-mix disparate sets of data and content into new digital objects. There is a sense amongst this group that “data is different” to other types of content, particulary in its diversity of types and re-uses. More generally there is the concern that anything that “smells of lawyers”, like something called a “license”, will have scientists running screaming in the opposite direction as they try to avoid any contact with their local administration and legal teams.

What I think was productive about the discussion on Tuesday is that we focused on what we could agree on with the aim of seeing whether it was possible to find a common position statement on the limited area of best practice for the publication of data that arises from public science. I believe such a statement is important because there is a window of opportunity to influence funder positions. Many funders are adopting data sharing policies but most refer to “following best practice” and that best practice is thin on the ground in most areas. With funders wielding the ultimate potential stick there is great potential to bootstrap good practice by providing clear guidance and tools to make it easy for researchers to deliver on their obligations. Funders in turn will likely adopt this best practice as policy if it is widely accepted by their research communities.

So we agreed on the following (I think – anyone should feel free to correct me of course!):

  1. A simple statement is required along the forms of  “best practice in data publishing is to apply protocol X”. Not a broad selection of licenses with different effects, not a complex statement about what the options are, but “best practice is X”.
  2. The purpose of publishing public scientific data and collections of data, whether in the form of a paper, a patent, data publication, or deposition to a database, is to enable re-use and re-purposing of that data. Non-commercial terms prevent this in an unpredictable and unhelpful way. Share-alike and copyleft provisions have the potential to do the same under some circumstances.
  3. The scientific research community is governed by strong community norms, particularly with respect to attribution. If we could successfully expand these to include share-alike approaches as a community expectation that would obviate many concerns that people attempt to address via licensing.
  4. Explicit statements of the status of data are required and we need effective technical and legal infrastructure to make this easy for researchers.

So in aggregate I think we agreed a statement similar to the following:

“Where a decision has been taken to publish data deriving from public science research, best practice to enable the re-use and re-purposing of that data, is to place it explicitly in the public domain via {one of a small set of protocols e.g. cc0 or PDDL}.”

The advantage of this statement is that it focuses purely on what should be done once a decision to publish has been made, leaving the issue of what should be published to a separate policy statement. This also sidesteps issues of which data should not be made public. It focuses on data generated by public science, narrowing the field to the space in which there is a moral obligation to make such data available to the public that fund it. By describing this as best practice it also allows deviations that may, for whatever reason, be justified by specific people in specific circumstances. Ultimately the community, referees, and funders will be the judge of those justifications. The BBSRC data sharing policy states for instance:

BBSRC expects research data generated as a result of BBSRC support to be made available…no later than the release through publication…in-line with established best practice  in the field [CN – my emphasis]…

The key point for me that came out of the discussion is perhaps that we can’t and won’t agree on a general solution for data but that we can articulate best practice in specific domains. I think we have agreed that for the specific domain of published data from public science there is a way forward. If this is the case then it is a very useful step forward.

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Why good intentions are not enough to get negative results published

There are a set of memes that seem to be popping up with increasing regularity in the last few weeks. The first is that more of the outputs of scientific research need to be published. Sometimes this means the publication of negative results, other times it might mean that a community doesn’t feel they have an outlet for their particular research field. The traditional response to this is “we need a journal” for this. Over the years there have been many attempts to create a “Journal of Negative Results”. There is a Journal of Negative Results – Ecology and Evolutionary Biology (two papers in 2008), a Journal of Negative Results in Biomedicine (four papers in 2009, actually looks pretty active) , a Journal of Interesting Negative Results in Natural Language (one paper), and a Journal of Negative Results in Speech and Audio Sciences, which appears to be defunct.

The idea is that there is a huge backlog of papers detailing negative results that people are gagging to get out if only there was somewhere to publish them. Unfortunately there are several problems with this. The first is that actually writing a paper is hard work. Most academics I know do not have the problem of not having anything to publish, they have the problem of getting around to writing the papers, sorting out the details, making sure that everything is in good shape. This leads to the second problem, that getting a negative result to a standard worthy of publication is much harder than for a positive result. You only need to make that compound, get that crystal, clone that gene, get the microarray to work once and you’ve got the data to analyse for publication. To show that it doesn’t work you need to repeat several times, make sure your statistics are in order, and establish your working condition. Partly this is a problem with the standards we apply to recording our research; designing experiments so that negative results are well established is not high on many scientists’ priorities. But partly it is the nature of beast. Negative results need to be much more tightly bounded to be useful .

Finally, even if you can get the papers, who is going to read them? And more importantly who is going to cite them? Because if no-one cites them then the standing of your journal is not going to be very high. Will people pay to have papers published there? Will you be able to get editors? Will people referee for you? Will people pay for subscriptions? Clearly this journal will be difficult to fund and keep running. And this is where the second meme comes in, one which still gets suprising traction, that “publishing on the web is free”. Now we know this isn’t the case, but there is a slighlty more sophisticated approach which is “we will be able to manage with volunteers”. After all with a couple of dedicated editors donating the time, peer review being done for free, and authors taking on the formatting role, the costs can be kept manageable surely? Some journals do survive on this business model, but it requires real dedication and drive, usually on the part of one person. The unfortunate truth is that putting in a lot of your spare time to support a journal which is not regarded as high impact (however it is measured) is not very attractive.

For this reason, in my view, these types of journals need much more work put into the business model than for a conventional specialist journal. To have any credibility in the long term you need a business model that works for the long term. I am afraid that “I think this is really important” is not a business model, no matter how good your intentions. A lot of the standing of a journal is tied up with the author’s view of whether it will still be there in ten years time. If that isn’t convincing, they won’t submit, if they don’t submit you have no impact, and in the long term a downward spiral until you have no journal.

The fundamental problem is that the “we need a journal” approach is stuck in the printed page paradigm. To get negative results published we need to reduce the barriers to publication much lower than they currently are, while at the same time applying either a pre- or post-publication filter. Rich Apodaca, writing on Zusammen last week talked about micropublication in chemistry, the idea of reducing the smallest publishable unit by providing routes to submit smaller packages of knowledge or data to some sort of archive. This is technically possible today, services like ChemSpider, NMRShiftDB, and others make it possible to submit small pieces of information to a central archive. More generally the web makes it possible to publish whatever we want, in whatever form we want, but hopefully semantic web tools will enable us to do this in an increasingly more useful form in the near future.

Fundamentally my personal belief is that the vast majority of “negative results” and other journals that are trying to expand the set of publishable work will not succeed. This is precisely because they are pushing the limits of the “publish through journal” approach by setting up a journal. To succeed these efforts need to embrace the nature of the web, to act as a web-native resource, and not as a printed journal that happens to be viewed in a browser. This does two things, it reduces the barrier to authors submitting work, making the project more likely to be successful, and it can also reduce costs. It doesn’t in itself provide a business model, nor does it provide quality assurance, but it can provide a much richer set of options for developing both of these that are appropriate to the web. Routes towards quality assurance are well established, but suffer from the ongoing problem of getting researchers involved in the process, a subject for another post. Micropublication might work through micropayments, the whole lab book might be hosted for a fee with a number of “publications” bundled in, research funders may pay for services directly, or more interestingly the archive may be able to sell services built over the top of the data, truly adding value to the data.

But the key is a low barriers for authors and a robust business model that can operate even if the service is perceived as being low impact. Without these you are creating a lot of work for yourself, and probably a lot of grief. Nothing comes free, and if there isn’t income, that cost will be your time.

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Thinking about peer review of online material: The Peer Reviewed Journal of Open Science Online

I hold no particular candle for traditional peer review. I think it is inefficient, poorly selective, self reinforcing, often poorly done, and above all, far too slow. However I also agree that it is the least worst system we have available to us.  Thus far, no other approaches have worked terribly well, at least in the communication of science research. And as the incumbent for the past fifty years or so in the post of ‘generic filter’ it is owed some respect for seniority alone.

So I am considering writing a fellowship proposal that would be based around the idea of delivering on the Open Science Agenda via three independent projects, one focussed on policy and standards development, one on delivering a shareable data analysis pipeline for small angle scattering as an exemplar of how a data analysis process can be shared, and a third project based around building the infrastructure for embedding real science projects involving chemistry and drug discovery in educational and public outreach settings. I think I can write a pretty compelling case around these three themes and I think I would be well placed to deliver on them, particularly given the collaborative support networks we are already building in these areas.

The thing is I have no conventional track record in these areas. There are a bunch of papers currently being written but none that will be out in print by the time the application is supposed to go in. My recorded contribution in this area is in blog posts, blog comments, presentations and other material, all of which are available online. But none of which are peer-reviewed in the conventional sense.

One possibility is to make a virtue of this – stating that this is a rapidly moving field – that while papers are in hand and starting to come out that the natural medium for communication with the specific community is online through blogs and other media. There is an argument that conventional peer review simply does not map on to the web of data, tools, and knowledge that is starting to come together and that measuring a contribution in this area by conventional means is simply misguided.  All of which I agree with in many ways.

I just don’t think the referees will buy it.

Which got me thinking. It’s not just me, many of the seminal works for the Open Science community are not peer reviewed papers. Bill Hooker‘s three parter [1, 2, 3] at Three Quarks Daily comes to mind, as does Jean-Claude’s presentation on Nature Precedings on Open Notebook Science, Michael Nielsen’s essay The Future of Science, and Shirley Wu’s Envisioning the scientific community as One Big Lab (along with many others). It seems to me that these ought to have the status of peer reviewed papers which raises the question. We are a community of peers, we can referee, we can adopt some sort of standard of signficance and decide to apply that selectively to specific works online. So why can’t we make them peer reviewed?

What would be required? Well a stable citation obviously, so probably a DOI and some reasonably strong archival approach, probably using WebCite.  There would need to be a clear process of peer review, which need not be anonymous, but there would have to be a clear probity trail to show that an independent editor or group of referees made a decision and that appropriate revisions had been made and accepted. The bar for acceptance would also need to be set pretty high to avoid the charge of simply rubber stamping a bunch of online material. I don’t think open peer review is a problem for this community so many of the probity questions can be handled by simply having the whole process out in the open.

One model would be for an item to be submitted by posting a link on a new page on an independent Wiki . This would then be open to peer review. Once three (five?) independent reviewers had left comments and suggestions – and a version of the document created that satisfied them posted – then the new version could be re-posted at the author’s site, in a specified format which would include the DOI and arhival links, along with a badge that would be automatically aggregated to create the index a la researchblogging.org. There would need to be a charge, either for submission or acceptance – submission would keep volume down and (hopefully) quality up.

How does this differ from setting up a journal? Well two major things – one is that the author remains the publisher so the costs of publication per se are taken out of the equation. This is important as it keeps costs down – not zero, there is still the cost of the DOI and (even if it is donated) the time of editors and referees in managing the process and giving a stamp of authority. The main cost is in maintaining some sort of central index and server pointing out at the approved items. It would also be appropriate to support WebCite if that is the backstop archive. But the big costs for journals are in providing storage that is stable in the long term and managing peer review. If the costs of storage are offloaded and  the peer review process can be self organised then the costs drop significantly.

The second major advantage is that, as a community we already do a lot of this, looking over blog posts, linking to presentations, writing commentary or promoting them on FriendFeed. The reason why ArXiv worked was that there was already a culture of preprints amongst that community. The reason why commenting, rating,  and open peer review trials have not been as successful as people had hoped is because there is no pre-existing culture of doing these things. We already have a culture of open peer review in our community. Is it worth formalising it for the really high quality material that’s already out there?

I am aware that this goes against many of the principles of open and continuous review that many of you hold dear but I think it could serve two useful purposes. First it means that members of the community, particularly younger members, can bolster their CV with peer reviewed papers. Come the revolution this won’t matter but we’re not there yet. Making these contributions tangible for people could be quite powerful. Secondly it takes the important material out of the constant stream of objects flitting past on our screens and gives them a static (I won’t say permanent) priviledged place as part of the record of this field.  Many of them perhaps already have this but I think there is a value in formalising it. Is it worth considering? This proposal is out for review.

 

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Can post publication peer review work? The PLoS ONE report card

This post is an opinion piece and not a rigorous objective analysis. It is fair to say that I am on the record as and advocate of the principles behind PLoS ONE and am also in favour of post publication peer review and this should be read in that light. [ed I’ve also modified this slightly from the original version because I got myself mixed up in an Excel spreadsheet]

To me, anonymous peer review is, and always has been, broken. The central principle of the scientific method is that claims and data to support those claims are placed, publically, in the view of expert peers. They are examined, and re-examined on the basis of new data, considered and modified as necessary, and ultimately discarded in favour of an improved, or more sophisticated model. The strength of this process is that it is open, allowing for extended discussion on the validity of claims, theories, models, and data. It is a bearpit, but one in which actions are expected to take place in public (or at least community) view. To have as the first hurdle to placing new science in the view of the community a process which is confidential, anonymous, arbitrary, and closed, is an anachronism.

It is, to be fair, an anachronism that was necessary to cope with rising volumes of scientific material in the years after the second world war as the community increased radically in size. A limited number of referees was required to make the system manageable and anonymity was seen as necessary to protect the integrity of this limited number of referees. This was a good solution given the technology of the day. Today, it is neither a good system, nor an efficient system, and we have in principle the ability to do peer review differently, more effectively, and more efficiently. However, thus far most of the evidence suggests that the scientific community dosen’t want to change. There is, reasonably enough, a general attitude that if it isn’t broken it doesn’t need fixing. Nonetheless there is a constant stream of suggestions, complaints, and experimental projects looking at alternatives.

The last 12-24 months have seen some radical experiments in peer review. Nature Publishing Group trialled an open peer review process. PLoS ONE proposed a qualitatively different form of peer reivew, rejecting the idea of ‘importance’ as a criterion for publication. Frontiers have developed a tiered approach where a paper is submitted into the ‘system’ and will gradually rise to its level of importance based on multiple rounds of community review. Nature Precedings has expanded the role and discipline boundaries of pre-print archives and a white paper has been presented to EMBO Council suggesting that the majority of EMBO journals be scrapped in favour of retaining one flagship journal for which papers would be handpicked from a generic repository where authors would submit, along with referees’ reports and author’s response, on payment of a submission charge. Of all of these experiments, none could be said to be a runaway success so far with the possible exception of PLoS ONE. PLoS ONE, as I have written before, succeeded precisely because it managed to reposition the definition of ‘peer review’. The community have accepted this definition, primarily because it is indexed in PubMed. It will be interesting to see how this develops.

PLoS has also been aiming to develop ratings and comment systems for their papers as a way of moving towards some element of post publication peer review. I, along with some others (see full disclosure below) have been granted access to the full set of comments and some analytical data on these comments and ratings. This should be seen in the context of Euan Adie’s discussion of commenting frequency and practice in BioMedCentral journals which broadly speaking showed that around 2% of papers had comments and that these comments were mostly substantive and dealt with the science. How does PLoS ONE compare and what does this tell us about the merits or demerits of post publication peer review?

PLoS ONE has a range of commenting features, including a simple rating system (on a scale of 1-5) the ability to leave freetext notes, comments, and questions, and in keeping with a general Web 2.o feel the ability to add trackbacks, a mechanism for linking up citations from blogs. Broadly speaking a little more than 13% (380 of 2773) of all papers have ratings and around 23% have comments, notes, or replies to either (647 of 2773, not including any from PLoS ONE staff) . Probably unsurprisingly most papers that have ratings also have comments. There is a very weak positive correlation between the number of citations a paper has received (as determined from Google Scholar) and the number of comments (R^2 = 0.02, which is probably dominated by papers with both no citations and no comments, which are mostly recent, none of this is controlled for publication date).

Overall this is consistent with what we’d expect. The majority of papers don’t have either comments or ratings but a significant minority do. What is slightly suprising is that where there is arguably a higher barrier to adding something (click a button to rate versus write a text comment) there is actually more activity. This suggests to me that people are actively uncomfortable with rating papers versus leaving substantive comments. These numbers compare very favourably to those reported by Euan on comments in BioMedCentral but they are not yet moving into the realms of the majority. It should also be noted that there has been a consistent  programme at PLoS ONE with the aim of increasing the involvement of the community. Broadly speaking I would say that the data we have suggest that that programme has been a success in raising involvement.

So are these numbers ‘good’? In reality I don’t know. They seem to be an improvement on the BMC numbers arguing that as systems improve and evolve there is more involvement. However, one graph I received seems to indicate that there isn’t an increase in the frequency of comments within PLoS ONE over the past year or so which one would hope to see. Has this been a radical revision of how peer review works? Well not yet certainly, not until the vast majority of papers have ratings, but more importantly not until we have evidence that people are using those ratings. We are not yet in a position where we are about to see a stampede towards radically changed methods of peer review and this is not surprising. Tradition changes slowly – we are still only just becoming used to the idea of the ‘paper’ being something that goes beyond a pdf, embedding that within a wider culture of online rating and the use of those ratings will take some years yet.

So I have spent a number of posts recently discussing the details of how to make web services better for scientists. Have I got anything useful to offer to PLoS ONE? Well I think some of the criteria I suggested last week might be usefully considered. The problem with rating is that it lies outside the existing workflow for most people. I would guess that many users don’t even see the rating panel on the way into the paper. Why would people log into the system to look at a paper? What about making the rating implicit when people bookmark a paper in external services? Why not actually use that as the rating mechanism?

I emphasised the need for a service to be useful to the user before there are any ‘social effects’ present. What can be offered to make the process of rating a paper useful to the single user in isolation? I can’t really see why anyone would find this useful unless they are dealing with huge number of papers and can’t remember which one is which from day to day. It may be useful within groups or journal clubs but all of these require a group to sign up.  It seems to me that if we can’t frame it as a useful activity for a single person then it will be difficult to get the numbers required to make this work effectively on a community scale.

In that context, I think getting the numbers to around the 10-20% level for either comments or ratings has to be seen as an immense success. I think it shows how difficult it is to get scientists to change their workflows and adopt new services. I also think there will be a lot to learn about how to improve these tools and get more community involvement. I believe strongly that we need to develop better mechanisms for handling peer review and that it will be a very difficult process getting there. But the results will be seen in more efficient dissemination of information and more effective communication of the details of the scientific process. For this PLoS, the PLoS ONE team, as well as other publishers, including BioMedCentral, Nature Publishing Group, and others, that are working on developing new means of communication and improving the ones we have deserve applause. They may not hit on the right answer first off, but the current process of exploring the options is an important one, and not without its risks for any organisation.

Full disclosure: I was approached along with a number of other bloggers to look at the data provided by PLoS ONE and to coordinate the release of blog posts discussing that data. At the time of writing I am not aware of who the other bloggers are, nor have I read what they have written. The data that was provided included a list of all PLoS ONE papers up until 30 July 2008, the number of citations, citeulike bookmarks, trackbacks, comments, and ratings for each paper. I also received a table of all comments and a timeline with number of comments per month. I have been asked not to release the raw data and will honour that request as it is not my data to release. If you would like to see the underlying data please get in contact with Bora Zivkovic.

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Avoid the pain and embarassment – make all the raw data available

Enzyme

A story of two major retractions from a well known research group has been getting a lot of play over the last few days with a News Feature (1) and Editorial (2) in the 15 May edition of Nature. The story turns on claim that Homme Hellinga’s group was able to convert the E. coli ribose binding protein into a Triose phosphate isomerase (TIM) using a computational design strategy. Two papers on the work appeared, one in Science (3) and one in J Mol Biol (4). However another group, having obtained plasmids for the designed enzymes, could not reproduce the claimed activity. After many months of work the group established that the supposed activity appeared to that of the bacteria’s native TIM and not that of the designed enzyme. The paper’s were retracted and Hellinga went on to accuse the graduate student who did the work of fabricating the results, a charge of which she was completely cleared.

Much of the heat the story is generating is about the characters involved and possible misconduct of various players, but that’s not what I want to cover here. My concern is about how much time, effort, and tears could have been saved if all the relevant raw data was made available in the first place. Demonstrating a new enzymatic activity is very difficult work. It is absolutely critical to rigorously exclude the possibility of any contaminating activity and in practice this is virtually impossible to guarantee. Therefore a negative control experiment is very important. It appears that this control experiment was carried out, but possibly only once, against a background of significant variability in the results. All of this lead to another group wasting on the order of twelve months trying to replicate these results. Well, not wasting, but correcting the record, arguably a very important activity, but one for which they will get little credit in any meaningful sense (an issue for another post and mentioned by Noam Harel in a comment at the News Feature online).

So what might have happened if the original raw data were available? Would it have prevented the publication of the papers in the first place? It’s very hard to tell. The referees were apparently convinced by the quality of the data. But if this was ‘typical data’ (using the special scientific meaning of typical vis ‘the best we’ve got’) and the referees had seen the raw data with greater variability then maybe they would have wanted to see more or better controls; perhaps not. Certainly if the raw data were available the second group would have realised much sooner that something was wrong.

And this is a story we see over and over again. The selective publication of results without reference to the full set of data; a slight shortcut taken or potential issues with the data somewhere that is not revealed to referees or to the readers of the paper; other groups spending months or years attempting to replicate results or simply use a method described by another group. And in the meantime graduate students and postdocs get burnt on the pyre of scientific ‘progress’ discovering that something isn’t reproducible.

The Nature editorial is subtitled ‘Retracted papers require a thorough explanation of what went wrong in the experiments’. In my view this goes nowhere near far enough. There is no longer any excuse for not providing all the raw and processed data as part of the supplementary information for published papers. Even in the form of scanned lab book pages this could have made a big difference in this case, immediately indicating the degree of variability and the purity of the proteins. Many may say that this is too much effort, that the data cannot be found. But if this is the case then serious questions need to be asked about the publication of the work. Publishers also need to play a role by providing more flexible and better indexed facilities for supplementary information, and making sure they are indexed by search engines.

Some of us go much further than this, and believe that making the raw data immediately available is a better way to do science. Certainly in this case it might have reduced the pressure to rush to publish, might have forced a more open and more thorough scrutiny of the underlying data. This kind of radical openness is not for everyone perhaps but it should be less prone to gaffes of the sort described here. I know I can have more faith in the work of my group where I can put my fingers on the raw data and check through the detail. We are still going through the process of implementing this move to complete (or as complete as we can be) openness and its not easy. But it helps.

Science has moved on from the days where the paper could only contain what would fit on the printed pages. It has moved on from the days when an informal circle of contacts would tell you which group’s work was repeatable and which was not. The pressures are high and potential for career disaster probably higher. In this world the reliability and completeness of the scientific record is crucial. Yes there are technical difficulties in making it all available. Yes it takes effort, and yes it will involve more work, and possibly less papers. But the only thing that ultimately can really be relied on is the raw data (putting aside deliberate fraud). If the raw data doesn’t form a central part of the scientific record then we perhaps need to start asking whether the usefulness of that record in its current form is starting to run out.

  1. Editorial Nature 453, 258 (2008)
  2. Wenner M. Nature 453, 271-275 (2008)
  3. Dwyer, M. A. , Looger, L. L. & Hellinga, H. W. Science 304, 1967–1971 (2004).
  4. Allert, M. , Dwyer, M. A. & Hellinga, H. W. J. Mol. Biol. 366, 945–953 (2007).