（汉英对照）
The politics of publication
PETER A. LAWRENCE
Peter Lawrence is at the MRC Laboratory of Molecular Biology, Cambridge CB2 2QH, UK. e-mail: pal@mrc-lmb.cam.ac.uk. He has edited the journal Development since 1976, served on the editorial board of Cell and EMBO J., authored many papers and reviewed many more.
Authors, reviewers and editors must act to protect the quality of research.
Listen. All over the world scientists are fretting. It is night in London and Deborah Dormouse is unable to sleep. She can't decide whether, after four weeks of anxious waiting, it would be counterproductive to call a Nature editor about her manuscript. In the sunlight in Sydney, Wayne Wombat is furious that his student's article was rejected by Science and is taking revenge on similar work he is reviewing for Cell. In San Diego, Melissa Mariposa reads that her article submitted to Current Biology will be reconsidered, but only if it is cut in half. Against her better judgement, she steels herself to throw out some key data and oversimplify the conclusions — her postdoc needs this journal on his CV or he will lose a point in the Spanish league, and that job in Madrid will go instead to Mar Maradona.
The decision about publication of a paper is the result of interaction between authors, editors and reviewers. Scientists are increasingly desperate to publish in a few top journals and are wasting time and energy manipulating their manuscripts and courting editors. As a result, the objective presentation of work, the accessibility of articles and the quality of research itself are being compromised.
One main cause
These trends are fuelled by the increasing pressure in biomedical science to publish in the leading journals. Even our language reflects this obsession — we say that Jim Jargon did well as a graduate student because he published a "Cell paper", illustrating that we now consider the journal to be more important than the scientific message. If we publish in a top journal we have arrived, if we don't we haven't.
Why has this happened? It is partly because, rather than assessing the research itself, those who distribute the money and positions now evaluate scientists by performance indicators (it is much easier to tot up some figures than to think seriously about what a person has achieved). Managers are stealing power from scientists and building an accountability culture that "aims at ever more perfect administrative control of institutional and professional life"1. The result is an "audit society"2, in which each indicator is invested with a specious accuracy and becomes an end in itself.
Evaluations of scientists depend on numbers of papers, positions in lists of authors, and journals' impact factors. In Japan, Spain and elsewhere, such assessments have reached formulaic precision. But bureaucrats are not wholly responsible for these changes — we scientists have enthusiastically colluded. What began as someone else's measure has become our (own) goal. Although there are good reasons for publishing papers where they are more likely to be read, when we give the journal priority over the science we turn ourselves into philistines in our own world.
Some scientists realize this, but why have most taken up the journal chase so enthusiastically? It has to do with both psychology and careerism. Young researchers see a paper in a good journal as their initiation into the scientific élite. The established seek publication in leading journals to certify their high opinion of themselves. All are learning that building capital in the hard currency of the audit society can be safer and easier than founding a reputation on discoveries. Another factor is that contemporary society has a craze for publicity, to which scientists are not immune. Many are gratified to find themselves or their work reported (accurately or not) in the media, and leading journals provide a route through press releases. El País, for example, usually features articles about any work by Spanish scientists published in Nature, Cell or Science.
Consequences
There are consequences for authors, editors and reviewers.
Authors have to decide when and how to write up their work. The ideal time is when a piece of research is finished and can carry a convincing message, but in reality it is often submitted at the earliest possible moment (two papers count for twice as much as one, never mind if the second paper mainly corrects errors in the first). Findings are sliced as thin as salami and submitted to different journals to produce more papers.
Work must be rushed out to minimize the danger of being scooped — top journals will not consider a paper if a similar result has appeared in a competing journal, even if the experiments have taken years and there is only a week or two of disparity. Yet it can be advantageous if rival papers are submitted at the same time, as each author can use the other paper to tempt editors into concluding that the topic is a hot one. This practice has led to many dangerous liaisons between competing groups. It is no wonder that agonizing over presentation as well as the timing of submission keeps many scientists awake at night.
Authors need to decide how to get their paper into a top journal. Can the results be hyped to make them look more topical? Are there some trendy stock phrases that can be used3? Would oversimplification add to the appeal? Could a lofty take-home message be made to fit? Can even a tenuous link to a human disease be found? (Mention of a human disease boosts the number of subsequent references to the paper and can make it more attractive to a journal.) Can the results be squeezed into a shorter format than they require? For example, can they be submitted as a brief Letter to Nature — even though a longer paper in a more specialized journal would be of greater service to readers? Letters to Nature and Reports in Science are often presented in such a compressed form with such minuscule figures that they can be hard to decipher. Supplementary online material may alleviate this problem, although readers of print editions may not find it convenient to look at, and people have concerns about the length of its electronic shelf-life.
Increasingly, such a high premium is put on presentation that the leader of a group (who has not done the experiments) writes the paper reporting work done by a junior scientist (who has). The team leader is more experienced and more able to present the work in the best possible light — and for this, a lack of knowledge of the details can be advantageous! The student or postdoc is released to go back to the bench, increasing productivity. However, she or he does not get taught how to write up results4.
Editors. It is no surprise that editors of élite journals receive many submissions. For example, Nature now receives around 9,000 manuscripts a year (double that of 10 years ago) and has to reject about 95% of biomedical papers. Development, a quality specialist journal, now rejects roughly 70%, compared with 50% in 1990. In leading journals there are too many submissions to send most out for peer review, so the editor's decision has become, quantitatively, much more important than the judgement of reviewers. Consequently, editors are courted by authors who resort to tactics such as charm offensives during "presubmission enquiries", networking at conferences and wheedling telephone calls — or pulling rank, using contacts, threatening and bullying. Group leaders can justify spending time and ingenuity on these stratagems — editors can be swayed and the rewards for success are high. Furthermore, impact factors and finance have joined forces to build up competition between top journals (Cell Press was recently sold for a great deal of money). One result is that editors are sent out to woo star scientists for their trendiest papers. These forces all combine to create an antiscientific culture in which pushiness and political skills are rewarded too much, and imaginative approaches, high-quality results and logical argument, too little.
Even experienced editors are on uncertain ground — sifting through a mass of diverse papers objectively and hurriedly is almost impossible. The advent of the Medline search and other Internet-based services has helped them, but it is still difficult to see clearly into the dark corners of specialization. Understandably insecure, editors play safe and favour the fashionable, familiar and expected over the flaky and unexpected — or original. Inevitably, mistakes are made. The original paper by Michael Berridge and Robin Irvine on phosphoinositol and signalling, which became the second most quoted article throughout the 1980s, was originally turned down by Nature. The authors fought back and it was accepted5. But when Berridge synthesized the information and added new ideas in another paper, it was rejected again by Nature, eventually published by the Biochemical Journal6 and became the fifth most quoted paper of the 1980s7.
Reviewers are, of course, authors wearing a different hat. There can be conflicts — for example, does the reviewer favour the work of a competitor and thereby endanger his or her student's career? Such opposing interests can explain why two reviewers of similar expertise sometimes present vastly different opinions about the same paper. It does not help that top journals are increasingly giving reviewers an extra task. Apart from the traditional technical and scientific assessments, where objective criteria are paramount, reviewers are now being asked to judge whether a manuscript constitutes a "Science" paper — is it sufficiently exciting to interest the "general reader"? This participation in editorial decisions gives reviewers opportunities to punish authors they do not like, settle old scores and hold up competitors. From many years of editing experience, I am persuaded that a minority of reviewers take advantage of these opportunities. Some bounce the same paper from more than one journal, making it more difficult for a less politically adept scientist to present his or her work, especially if it goes against the current grain. Objectivity is also threatened by a tacit understanding between some leading scientists: they invite each other onto committees, to conferences, nominate each other for prizes and awards, and support publication of each other's papers.
Another relatively recent phenomenon is the practice of sending papers to three reviewers. Although this is partly to ensure that at least two reviews are received, I think it is also so that the advice received cannot be a tie. Decision by vote can encourage rejected authors to make empty appeals, praising favourable reviewers, denigrating negative ones and asking for new reviewers — in the hope of getting another plus. Rejection is easier to accept if there is a thoughtful reason for it from which one can learn.
Hard-pressed editors take power from authors and hand it to reviewers in other ways. Reviewers often ask for changes and new experiments, even though they may be rather ignorant of the details and may have formed an opinion of the paper in half an hour. Nevertheless, the easiest and most commonly chosen course for the editor is to ask the authors to "satisfy" all of the reviewers, then send the revised manuscript for reassessment. If authors have well-founded disagreements with a reviewer, they find themselves in a dilemma: do they invest time in experiments they do not believe will help, do controls that few other informed people would find important, or even draw conclusions that are not theirs? If they do not, reviewer X may not be appeased and the editor would be unswayable. In former days, these authors could have solved their problems by sending their papers elsewhere, but now that the journal itself has become so important to their careers, they feel forced to comply. In this situation the reviewers can become more like censors than assessors. I have seen many examples of this and, sometimes, months of research time have been misspent, even to the extent that an author can be scooped in the interim.
Faster publication times, materials-transfer agreements and threats of legal action to force journals to identify reviewers have added to the pressure. In the case of faster publication times, journals can offer chosen authors fast-track treatment and advanced online publication, helping them to steal a march on competitors. A reviewer can use information and may have time to modify his or her own manuscript and even publish it elsewhere first. Temptation and suspicion have heated up enough to melt the wall of confidentiality that reviewers owe to authors. Still, I believe there is genuine confusion about the level of confidentiality that reviewers should adopt. Is the reviewer obliged not to reveal even the existence of a submitted manuscript to anyone? I think so, but do we all concur? Should a reviewer agree to assess a paper that he or she has already advised another journal to reject? I think not, but this happens frequently.
Cures?
It is no wonder that authors are becoming paranoid. Roughly half of the submission letters I now receive request me not to use certain reviewers, often because of "conflicts of interest". Behind this phrase lurks the fear of misuse of the information in the paper — although admittedly it is sometimes a ploy to avoid the sharp-eyed and critical.
My main purpose here is consciousness raising. But we can all start to improve things by toning down our obsession with the journal. The most effective change by far would be if the organizations that award grants and manage research programmes were to place much less trust in a quantitative audit that reeks of false precision. Such organizations have the big advantage of hindsight — unlike editors and reviewers at the time of submission, they can ask themselves if key papers published by the candidate are illuminating, have proved influential and whether their main results have been confirmed by others.
Authors can help to break up the cult of the journal. One way is to set up mutually supportive alliances, as has been done for the field of cell signalling http://www.signaling-gateway.org). If established authors start to publish selectively in open-access websites and in specialized journals when appropriate, a better example would be set for younger scientists. This would reduce the enormous pressure on the leading journals, which then could again begin to publish more comprehensible papers that tell a complete story, perhaps even bringing the 'general reader' back to life.
I am not suggesting sweeping changes to the review process. For example, I don't think a change to open peer-reviewing (as discussed in ref. 8) will help, mainly because younger reviewers would be intimidated and the political power of the established would be increased. One change which would now be feasible through online submission of two forms of the manuscript, would be to deny the reviewers authors' names. It is crucial that the responsibilities and duties of reviewers are clarified and made more public. For example, they could be better educated about confidentiality by the journal, along the lines of Nature's advice http://www.nature.com/nature/submit/policies/index.html#8).
Professional editors need to be more aware of these dangers. They now have to make difficult decisions that are of vital importance to authors, far beyond the publication or not of a particular paper, as well as meeting rejection rates as high as 95%. They have — perhaps understandably — been relinquishing too many of their responsibilities to reviewers. It does not help that editors may not have had enough experience of research and lack hands-on knowledge, particularly outside one narrow subject area. They need to act now to reinstate authors' rights. Once a decision has been made to publish in principle, they should never simply demand in a blanket sense that authors satisfy reviewers X, Y and Z, but should interpret referees' advice and be willing to accept reasoned discussion about aspects of the referees' criticisms. Editors should then be in a decision to adjudicate among themselves or to seek further opinion from an expert who is given both sides of the argument. Editors should appreciate that, unlike the authors whose names are out there, anonymous reviewers will not be held to account if they make a mistake. It should always be remembered that the proper role of the reviewer is to advise the editor, not to gain control over the author's paper.
Editors should also take a more long-term and broader view about what is of interest, and act positively to encourage new approaches and topics in an affirmative action against fashion.It is fashion that makes looking for new members of signalling pathways into the hottest of current topics, which can lead to unnecessary duplication. Just one example — no less than four independent studies on the same new gene (pygopus), each describing years of careful and hard work by several people, have just been published (see ref. 9 and references therein).
As authors, we have abandoned the attempt to make our experimental papers accessible or comprehensible to the nonspecialist, often writing undiluted mixtures of hype and jargon. This is partly because we are writing in shorthand to fit our papers into a small space, and partly because we are trying to con the editors. But why not write papers that are readable, reduce the number of acronyms and gobbledeegook, and put methodological details in supplementary material on the web?
It is we older, well-established scientists who have to act to change things. We should make these points on committees for grants and jobs, and should not be so desperate to push our papers into the leading journals. We cannot expect younger scientists to endanger their future by making sacrifices for the common good, at least not before we do.
(Nature, 422, p259. 20 March 2003)
听着：世界各地有很多科学家都如生活炼狱之中，倍受煎熬。伦敦已是深夜， Deborah Dormouse依然辗转难眠。她已经焦急地等待了4周，她不知道如果她打电话给 《自然》杂志的编辑询问她的论文处理情况是否会产生负效应。在阳光灿烂的悉尼， Wayne Wombat正在大发雷霆，因为他的学生的论文被《科学》杂志拒绝了，《细胞》杂 志正在请他审阅一篇内容相似的论文，他要对之实施报复。在旧金山，Melissa Mariposa阅知她递交给《当代生物学》的论文必须缩减一半后才能被重新考虑。她不得 不忍痛删除一些关键数据，并且极端简化结果，因为她的博士后需要将这一期刊列在他 的简历上，否则他就得不到西班牙马德里的一个工作。
一篇论文是否能发表取决于作者、编辑和审稿人之间的相互作用。越来越多科学家们 正在孤注一掷地只将论文投递到少数几个顶尖的期刊，然后又浪费时间和精力去处理论 文，讨好编辑。这种做法最终危害了论文发表的目的、文章的可获得性和研究质量本身。
一个主要原因
在生物医学科学领域，日益加大的压力迫使科学家们将论文发表在顶级期刊上，更是 助长了这种趋势。甚至在我们的日常言语里也反映出对顶级期刊的迷恋 - 我们说某人 是一位好研究生，是因为他在《细胞》上发表了一篇论文。这说明我们认为期刊比科学 信息本身更重要性。这意味着如果我们在顶尖期刊上发表论文，我们的目标就达到了， 否则我们就失败了。
为什么会有这样的事情发生呢？部分原因是掌握经费和职位分配大权的人在
评价科学 家时不是评价研究本身，而是根据“表现指数”来衡量，因为将一些数字加起来比严肃 地思考一个人的成就更容易。管理者正在窃取科学家们的权力，他们营造出“成绩责任 制”文化，目的是建立最完善的行政管理体制，有效地控制研究机构和研究人员。结果， 这使得社会成为了一个“审计社会”（Audit society）：每一项指标都被精确地计算， 最后指标成为目的本身。
在这样的“审计社会”中，发表论文的数量、作者在名单中的排序和期刊的影响因子 成为评价科学家的依据。在日本、西班牙和世界其它地方，这种评价方式发展到成为精 确的公式化行为。但是，不能让行政管理人员对此全部负责，很多科学家们热情地参与 其中。从什么时候开始一些人为的指标成为科学工作的目标？尽管有各种堂皇的理由说， 将论文发表在顶尖期刊上会有更广泛的阅读量，但是，当我们将期刊的重要性置于科学 本身之上时，我们就是将我们在自己的世界中变成了俗气和无教养之辈。 (我们就是将 自己在学术界置于平庸之辈。)
一些科学家已经意识到这个问题，但为什么绝大多数科学家还是如此热衷于期刊的名 望呢？这里有心理和职业两个方面的原因。年轻的科学家们将在好期刊上发表一篇好论 文视为进军科学皇冠的起点。而已有声望的科学家则希望在顶尖期刊上发表论文以证明 自己仍有高见。与在科学发现的王国中树立声望相比，所有的人都逐渐认识到，在当今 实实在在讲求硬通货的审计社会中聚集“资本”更为安全和容易。另外一个因素是现在 的社会疯狂地追求知名度，科学家们也身不由已。许多科学家在自己的工作被媒体报道 （无论准确与否）时会心存感激，而那些领头的杂志也通过新闻发布来为此铺平道路。 比如说，西班牙的大报El Pais就经常会对西班牙科学家在Nature，cell和Science上发 表的任何文章进行特别报道。
后果
这对于作者、编辑和审稿人的行为带来了一系列的后果。
作者必须决定什么时候、怎么写他们的研究工作。写论文的理想的时刻是在 某一研究工作告一段落，并获得了可信服的信息之时。但是，现实的做法常常是在有可 能出现结果的最早时候就开始写作。结果，科学发现就像意大利香肠一样被切成一片片， 然后再递交给不同的期刊以发表更多的论文。
科学家们必须全力以赴以最快的速度做出工作，以尽量减少论文被拒的风险。顶尖期 刊绝不会考虑竞争对手已经刊登过的结果相似的论文，即使这项研究已经花费数年时间 而递交的时间只相差一周或二周。当然，如果两篇竞争性的文章同时递交给期刊也有好 处，每位作者都会用另外一篇论文来引起编辑的注意，认为他们的研究课题是热门的。 毫无疑问，论文的递交和报告让许多科学家们彻夜难眠。
作者需要决定怎样做才能将他们的论文发表在顶尖期刊上。研究结果是否可以被炒作 到足以为话题？是否要将一个复杂的问题超级简化以吸引人？是否可以在论文中找到一 个故弄玄虚的信息让人们立刻记住？是否发现了与人类疾病有关的某个含糊不清的联系？ （提及人类疾病往往会提高以后论文的引用数量，也使杂志显得有吸引力。）能否将论 文的长度压缩到实际需求的更短？比如，即使论文应该以更长的形式递交到更专业化期 刊上，为读者提供更多些的服务。是否可以将它压缩成更短的形式而递交到Nature杂志？ Nature上的短文和Science上的报告部分常常压缩很大，只有很不显眼的示意图，使得 其内容难以被读者***。互联网上的补充材料也许可以缓解这一问题，但是印刷版的读 者会觉得上网不是那么方便，而它们的电子版的上架时间也让人担心。
这样，越来越多的研究小组负责人开始亲自执笔写论文，他们或许并没参与实验，而 实验工作主要是由初级科学家完成的。但是，研究组长经验丰富，知道如何以最好的方 式展示工作，也许正因如此，对实验细节的不了解反倒成为有利因素。学生和博士后又 回到了桌边努力工作，增加产出。然而，他们却没有学会如何写作研究报告。
编辑： 顶尖期刊的编辑总会收到过多的投稿。比如，《自然》杂志现在一年要 收到9000分左右的稿件，(这个数字是10年前的2倍)，因此不得不拒绝约95%的生物医学 方面的论文。《发育生物学》是一本高质量的专业期刊，它的拒稿率基本上是70%，而 在1990年，这一数字是50%。顶级的期刊收到太多的稿件，没有办法将它们都送给同行 进行评审，因此，编辑手中的权力变得比审稿人的判断重要得多。结果，作者们开始用 各种手段拉拢、奉承、甚至威胁编辑。小组组长能够证明花费时间和才智在这些策略上 是值得的，因为编辑们会因此动摇，而成功的回报非常之高。影响因子和经济的合力作 用在顶级期刊间建立起竞争（Cell杂志最近就以极高价格被转手）。这样的一个结果就 是编辑甚至会央求明星科学家为期刊写最流行的论文。所有这些力量综合在一起创造了 一种反科学的文化，出风头和***手腕会受到更高的回报，而富有想象力的方法、高质 量的研究结果和理性的争论却变得无足轻重。
即使是经验丰富的编辑也难于作出准确判断：要在一大堆各色论文中进行客观、快速 的筛选基本上是不可能的。以英特网为基础的服务能够为编辑提供一些帮助，但是，在 专业化的黑暗角落中看清实质问题仍然是困难重重。为了安全、稳妥起见，编辑们更喜 欢那些流行的、熟悉的和意料之中的结果，而不是那些看起来古怪的、意料之外的、或 者是原创性的结果。错误因此出现。Michael Berridge和 Robin Irvine一篇有关磷酸 肌苷和信号的原始性论文，在20世纪80年代成为引用率第二高的论文，但最初《自然》 杂志拒绝了这篇论文。作者奋起反抗，最终被接受。但是，当Berridge将一些信息综合 起来，再加上一些新观点形成另一篇论文时，他再次遭到《自然》杂志的拒绝，尽管最后这篇论文在《生物化学》杂志上发表，在80年代引用率最高的论文中排名第5位。
审稿人：审稿人当然也是论文作者，只是戴上了不同的帽子。冲突因此不可避免， 比如，审稿人会支持竞争者的工作而让自己学生的职业处于危险境之中吗？这种利益的 冲突可以解释为什么同一领域的两位审稿人对同一篇文的评价有天壤之差。使得事情 更糟的是，顶尖期刊的编辑还会给审稿人额外的任务。在传统的科学和技术的评价中， 客观标准是至高无上的，除此之外，审稿人现在被要求对一篇论文是否算得上是一篇可 以发表在“《科学》”期刊的论文，即是否是让“大多数读者有兴趣”的论文作出判断。 让审稿人参与到编辑决策过程中的做法，给审稿人有机会去损害他们所不喜欢的作者、 了结宿怨、拖延竞争对手的工作。从我多年的编辑经历来看，的确有少数的审稿人把握了这种机会。还有一些审稿人让论文在好几个期刊之间转来，让那些缺乏***手腕的科 学家发表工作尤为困难，尤其是在研究结果与现有知识不同时。一些占主导地位的科学 家们彼此间达成默契：他们互相邀请对方加入委员会，在会议上相互提名对方获奖，支 持对方论文的发表等，科学的客观性因此受到了威胁。
最近另外一个相关的现象是将论文送给三位审稿人评审。尽管这样做部分是为了保证 至少会收到两份评审意见，但我认为这样做主要是为了保证不至于得到平局。投票做出 的决定鼓励被拒绝的作者做空洞的申诉，赞扬支持他们的审稿人，诋毁持负面意见的审 稿人，并要求新的审稿人，以期得到新的支持。
重压之下，编辑将作者的权力以另一种方式交给评审人。即使审稿人可能忽略了相当 的细节，并且可能是在半个小时内形成对一篇论文的意见，但他们通常总要求作者进行 修改或做新的实验。然而，对编辑来说最容易和最常见的选择就是让作者满足所有的审 稿人，再将修改后的论文送给他们重新评审。如果作者有充足的理由不同意审稿人的意 见，那么他就会处于两难境地：他们要么是花时间做他们认为很可能是无益的实验，或 者得出并不是他们自己的结果所支持的结论。如果他们不这样做，那么不知名的审稿人 的不满没有得到平息，编辑将坚持原来的观点。以前，这些作者会将他们的论文到处发 送，但是现在期刊变得如此重要足以影响他们的职业生涯，他们不得不屈从。在这种情 形下，审稿人更像是一位检查官而不是评价人。这种情况我见得太多，有时，研究人员< 会因此浪费数月的研究时间，而其间还有可能被别人抢先发表了论文。
更快的发表时间、材料交换的协议，以及被威胁告上法庭迫使期刊公开审稿人的名字， 各种压力在不断增加。因此出现为了更快的出版时间，一些期刊为某些特选的作者提供 绿色通道，提前在网上发表论文，帮助他们在时间的竞争中抢先一步，击败竞争对手。 而一些审稿人可能利用他所审论文的信息，拖延别人的时间来修改自己的论文，甚至在 别处抢先发表自己的论文。诱惑和怀疑堆积起来，融化了审稿人本来就应该使论文作者 对之加以信任的厚墙。我相信审稿人对自己应该采取的保密程度的理解存在真正的混乱。 审稿人是否应该遵从不向任何人透露一份稿件存在的保密原则？我认为应该，但我们是 否都遵从了呢？审稿人是否应该同意审阅一份自己已经建议另一份期刊拒收的稿件的要 求呢？我认为他不应该同意，但这种事情却时常发生。
对症下药
毫不奇怪，作者正变得越来越敏感而多疑。在我所收到的论文中，大约有一半的作者 要求不要将论文送交某审稿人，主要原因是“利益冲突”。但潜词却是担心论文中的信 息被误用，实际上他们也承认有时是为了避开严厉的眼睛和批评。
我此处的主要目的是提高大家对现状的认识。不过，我们可以开始共同努力来改进局 面，缓和对期刊的迷信。而最有效的变化是管理机构在决定经费和项目时不要再相信那 些充满错误的审计数据。与收到稿件的编辑和审稿人相比，这些机构具有事后诸葛亮更 全面认识事情的机会。他们可以自问，项目候选人所发表的关键性论文是否具有科学上 的启发性？是否被证明具有影响力，其主要结果是否已被其他人证实？
作者也有助于打破对期刊的顶礼膜拜。方法之一就是建立互相支持的联盟，比如在细 胞信号传导领域所作的那样http://www.signaling-gateway.org）。如果已有建树的 科学家推动将论文恰当地发表开放式网站上或专业化的期刊上（而不是像Nature 或Science这样的非专业期刊上），就将为年轻的科学家们树立一个好榜样。这样也会 减轻顶级期刊面临的巨大压力，从而使得这些期刊能够开始发表更完整的论文，方便读 者阅读理解，从而也真正挽回“一般读者”。
我并不建议大刀阔斧地改革审稿过程。比如，我并不认为开放的评审会有什么帮助， 主要原因是年轻的审稿人会受到威胁，而已有建树的科学家的影响力会更为增强。一个 可行的措施是在网上递交两份论文，使得审稿人不知道作者的名字。但关键问题是要明 确审稿人的责任和义务，并公诸于众。
专业的编辑更要明白这些危险。他们不得不艰难地做出对作者至关重要的决定，在拒 稿率高达95%的情况下，做出这种决定尤为不易。可以理解的是，也许编辑们已经将许 多本来属于他们的责任推给了审稿人。编辑们也许没有足够专业研究背景、并缺乏第一 手知识，特别是某一狭窄领域的知识，但这种推委于审稿人的做法是无济于事的。编辑 们应该立即行动起来，重新确立作者的权利。一旦决定发表一篇论文，编辑绝不能简单 地要求作者满足X、Y、Z审稿人的意见，而是解释审稿人的建议，并乐意接受理性的批 评和讨论。编辑们应该在自己之间做出决定，或者在给予双方意见的前提下寻找进一步 的专家意见。编辑应该充分意识到，与署名的作者不同的是，匿名的审稿人不会为自己 的错误负责。编辑应该始终牢记的是：审稿人的作用是向编辑提出建议，而不是获得作 者论文的任何控制权。
在关于学术重要性的问题上，编辑们应该具有更为长期和宽阔的眼界，并且通过对与 潮流不一致的研究内容的肯定性行为，来积极正面地鼓励新颖的方法和课题。潮流导致 寻求新的细胞信号传导成为目前最流行的研究论题，这会造成了不必要的重复性工作。 一个不幸的例子是，最近发表的四篇独立研究论文，就是关于一个相同的新基因 （pygopus基因）的重复工作，每一篇论文都纪录了多人在数年里的细致和艰苦的工作。
作为作者，我们放弃了让非专业人士也能阅读和接触我们论文的努力，文章中夹杂着 泡沫和术语。部分原因是我们以速记的方法记录我们的工作，让论文可以放入狭小的版 面。但是，为什么不让文章更有可读性，减少首字母的缩写和浮夸的语言，将详细的方 法和补充材料放到网上呢？
现在是我们这些年纪大的、已有建树的科学家们行动起来改变现状的时候。在有关经 费和工作职位的委员会上，我们应该确立重要的原则，不要再如此绝望地一味迫使论文 发表在顶级期刊上。我们不应该期望年轻的科学家们为了科学界共同的利益而冒着失去 个人前途的危险去呼吁变革，至少我们不应该让他们在我们之前牺牲自己。