研究方法 | 研究选题：如何在顶级管理学期刊发表论文（一）
The following article is from 南开管理评论 Author Jason 等
研究选题：如何在顶级管理学期刊发表论文（一）
重要性：迎接“大挑战”
在选择一个选题时要考虑的一个起点是研究是否面临或有助于一个巨大的挑战。“大挑战”一词是数学家大卫·希尔伯特（David Hilbert）的功劳，自20世纪初以来，他的一系列未解决的重要问题鼓励了数学研究的创新。在自然科学、工程和医学的各个领域都面临着巨大的挑战。美国国家工程院使用的重大挑战的例子包括开发更好的药物和使太阳能更加经济。其中最重大的挑战反映在联合国消除全球贫穷、疾病和饥饿的千年发展目标中。一项重大挑战的基本原则是追求大胆的想法，并采用较不传统的方法来解决悬而未决的大问题。
当然，很少有AMJ等管理学期刊的投稿会涉及像减少贫困或消除饥饿这样具有全球意义的议题。AMJ的文章能够做的是处理某一特定文献或研究领域中尚未解决的大问题，并以超越现有解释的大胆和非传统的方式解决这些问题。这一飞跃往往会产生新的范式，或为学术讨论开辟新的领地。例如，Ferlie、Fitzgerald、Wood和Hawkins（2005）提出了一个巨大的挑战：为什么基于证据的创新没有在医疗行业中传播。创新扩散在许多文献中都是一个非常重要的问题，而对医疗创新的关注也为这一话题增加了分量。Ferlie等（2005）就以一种大胆和非传统的方式面对这个话题，超越了线性扩散模型，并认为那些看似有助于扩散的因素——比如专业化——反而会造成“非扩散”。
这种对重大挑战的概念化，为融合理论有用性讨论，并从一个更宽泛的视角——个人、社会从经济和创业活动中获益，提供了一个熔炉（Brief & Dukerich，1991；Ghoshal，Bartlett，& Moran，1999；Schumpeter，1942；Sen，1999）。可以理解的是，不是每一个选题都能引入新的范式；学术的积累和社会科学的进步要求我们在前人工作的基础上再接再厉。此外，未解决问题的“宏大性”会随着时间的推移因文献的积累而变化。尽管如此，审视宏大挑战框架内的每一个议题，是确定研究选题的正确打开姿势；它允许作者阐明自己的研究是如何解决这个大问题中的一小部分的，并在这样做的同时，以严谨和相关性推进该领域的研究（Gulati，2007）。
新奇：改变对话
与许多其他顶级期刊一样，AMJ也强调选题的新颖性。鉴于科学研究可以被视为学者之间的对话（Huff，1998），检查选题新颖性的一个简单方法是考虑这个研究是否会改变已经在给定文献中发生的对话。这项研究是仅仅增加了现有声音的强度，还是在谈话朝着一个全新的方向飞驰时，会导致人们的头脑转向？有时，新的方向是通过在对话中加入新的词汇，以新的想法或结构的形式创造出来的；有时，新的方向仅仅是来自新的见解，而不是由先前的声音表达出来的。
新颖的选题往往是知识重组的结果，通过在两个文献或学科之间架起一座桥梁，创造出一些“新”的东西。随着时间的推移，从自身内部汲取灵感以扩展思想的领域往往变得更加孤立，从而降低了出现新鲜解决方案的可能性（George，Kotha和Zheng，2008）。组织理论和战略文献通常将“知识重组”看作产生新思想的途径。前提是，组织通过探索新的技术领域来获得灵感，并重新组合已经存在于组织中的知识所产生的想法，从而产生新的和创造性的解决方案（例如，March 1991；Rosenkopf和Nerkar，2001）。在这一论点的延伸中，Ahuja和Lampert（2001）发现组织必须克服三种创新突破学习的“病理”：倾向于喜欢熟悉的人而不是不熟悉的人，倾向于喜欢“老人”而不是“新人”，倾向于喜欢与现有方法近似的解决方案，而不是全新的。
这三种被称为“熟悉陷阱”“成熟陷阱”和“接近陷阱”的病理学在为AMJ选择选题时成为值得考虑的因素。选择一个过于熟悉的话题，可能会导致一项研究充其量被认为是现有谈话的边缘延伸。选择一个过于成熟的话题会引起人们对一个被认为过于多余的贡献的担忧。同样，代表与现有文献相邻领域的主题选择也可能被视为过于重叠，或者从现有的核心现象视角出发，偏离得过于彻底。Agarwal、Echambadi、Franco和Sarkar（2004）对“衍生公司”的研究代表了一个避免熟悉、成熟和接近陷阱的主题。衍生公司（Spin out）是一家公司的前雇员创办的创业企业，他们利用从公司历史中获得的知识，在同一领域继续竞争。Agarwal等人（2004）的研究通过关注一个新的和未被充分研究的现象，改变了创业和能力文献中的对话。
好奇心：吸引和保持注意力
尽管一个新奇的选题可能会吸引读者，但要吸引和保持他们的注意力还需要更多的东西。AMJ的最佳选题必须能够激发和维持好奇心。在这种情况下，好奇心可以被看作是一种方法导向的动机状态，与更深入、更持久和更沉浸式的信息处理相关（Kashdan & Silvia，2009）。戴维斯（1971）“有趣指数”是描述如何激发读者好奇心的一种有用方法。戴维斯认为，当选题的命题与读者认为理所当然的假设背道而驰时，选题才是有趣的。例如，一项研究揭示一个看似好的现象其实是坏的，会引起好奇心，因为它挑战了读者最初的期望。
另一种激发和保持好奇心的方法可用“谜”来比喻。Alvesson等（2007）认为，有趣的研究选题来源于“故障”：在自己的数据或现有文献中令人惊讶的发现，这些发现无法用方法论问题或现有的解释来解释。“故障”为学者们提供了一个发挥想象力的机会，同时也预示着一个“谜”的潜在存在：“当问更多的问题时，游移……走到图书馆去读更多的书是不够的，一个谜团就在眼前”（Alvesson，2007:1272）。有趣的选题就产生于要解决或重新考量这种“谜”的欲望。据信，此类选题比更典型的“填补空白”方法更能引起人们的兴趣，从而产生研究问题（Alvesson & Sandberg，2011）。
事实上，我们可以通过思考为什么悬疑小说如此吸引人和引人入胜，将“谜”的比喻更进一步。想想阿加莎·克里斯蒂的《无人生还》，十个客人发现自己被困在一座岛上的豪宅里，然后按照“十个小兵”的童谣，一个接一个地被谋杀。这个故事之所以引人入胜，原因很简单：读者不知道结局。不幸的是，从标题上看，许多AMJ投稿的结尾是清晰而明显的，即使没有典型学术摘要中提供的“捣乱”，因为只有一个结论似乎是可信的。考虑一下这个标题：“领导者表现出的快乐对团队绩效的影响”，由于主题的直观性，审稿人可以猜测结尾的内容，或者至少猜测结果部分的内容。Van Kleef，Homan，Beersma，Van Knippenberg，Van Knippenerg和Damen（2009）的一项研究引起了更多的好奇心。在对领导者情绪表现的正面和负面影响不一致的研究结果的激励下，作者研究了领导者表现出快乐或愤怒是否会促进团队绩效。他们还研究了这些影响是否可以用追随者的情绪（“灼热的情感”）或追随者对表现的推断（“冷淡的算计”）来解释。哪种领导展示更有效，哪种机制解释结果？如果你猜不出结局，那么作者就做出了一个有效的选题安排。
范围：撒张宽网
如果研究范围太小，即使是最好的选题主意也会被破坏。我们的讨论将范围定义在相关结构、机制和视角方面，对选题中涉及的“景色”进行充分采样的程度。如果研究的范围不够宏大，就无法应对巨大的挑战，而撒下一张狭窄的网则限制了对相关谜团或文献空白的研究。提交的文章没有足够的范围，可能因为作者们错误地认为AMJ仍在发表“研究笔记”。事实上，AMJ并没有，也很少发表任何篇幅明显短于40页（用Microsoft Word表示）的文章（这是我们AMJ的一个指导原则）。我们也质疑一些文章在范围问题上的挣扎，因为作者将数据切得太细，试图从一个数据集中获得多篇好的论文，而不是一篇绝好的论文。
最好的选题是对给定领域中的“景色”进行全面、综合的采样，甚至可能包括使用通过多个视角获得的结构和机制。Seibert，Kraimer和Liden（2001）的社会资本和职业成功审视，为有效范围内的选题提供了一个很好的例子。关于社会资本的讨论指出了三个理论观点，可以解释为什么员工的社会网络的规模和组成会影响其工资、晋升能力和职业满意度。Seibert等人（2001年）本可以选择把重点放在第一种观点上，或者放在第二种观点上，或者放在第三种观点上。相反，他们把重点放在所有三个方面，在每一方面都加入了调节变量。当然，如此一来，文章可能过长。然而，这些问题可以在修订版中解决，因为审稿人可以建议删除变量，以便将更多的焦点放在某个话题上。
可操作性：实践的洞察力
最后，一个选题应该是（在实践上）可操作的：它应该为管理或组织实践提供见解。一种接近可操作性标准的方法是考虑实践中的可变性，这是我们现有的结构词汇无法解释的，也就是说，我们的学术语言或词汇让我们失望的地方。例如，创新文献通常将创新描绘为资本密集型研发努力的结果。那么，我们如何解释资本密集度低、研发支出严重受限，但仍能创造价值的新兴创新？20美元的人工膝关节和低成本医疗设备等产品在竞争和学术意义上都是“空白”，因此，对这些选题的学术研究具有内在的可操作性。
McGahan（2007）指出了增强管理研究可操作性的五种主要方式：（1）提供反直觉的见解，（2）强调新的和重要的实践的影响，（3）展示实践的不一致性和后果，（4）建议一个特定的理论来解释一个有趣的和当前的情况，以及（5）确定标志性现象，开辟了新的研究和实践领域。当选题代表着巨大的挑战，当他们的追求在范围上雄心勃勃，并为现有对话提供新颖和非传统的改变时，所有这五条路径才会存在且坚实。Vermeulen（2007）提供了一个补充的视角，他指出，当研究能够产生实践者认为有助于理解自己的组织现实的见解时，特别是当研究涉及管理者控制范围内的变量时，研究才会具有相关性。
结论
总而言之，一个有效的选题让研究者能够应对文献中的巨大挑战，追求激发和保持好奇心的新方向，建立一个有雄心壮志的研究范围，并发现可操作的见解。AMJ的外审们目前掌握的64篇评论文章，如果它们的选题具有这样的特质，而不是更谦虚、渐进、直观、狭隘或不相关的性质，那么它们的表现会更好。考虑到选题是任何投稿中最不可能被修改的方面之一，我们将建议任何未来的作者就其选题向坦率和挑剔的同事们征求反馈，特别是如果这些同事熟悉AMJ。这样做可以帮助这些选题形成一种势头（momentum），一旦稿件交给审稿人，这种势头将在今后的道路上有所帮助。
作者：Jason A. Colquitt，Gerard George
校译：《南开管理评论》编辑部
原文出处：Academy of Management Journal 2011, Vol. 54, No. 3, 432–435.。
英文原文：
FROM THE EDITORS
PUBLISHING IN AMJ—PART 1: TOPIC CHOICE
At the moment of this writing, there are 64 submissions in the hands of AMJ reviewers, who have been asked to critically evaluate the merits of those submissions relative to the mission and goals of the Journal. Although those reviewers will read their assigned manuscripts are fully and thoughtfully, their recommendations to the action editor will depend, in part, on a choice made years earlier: the topic of the study. The seeds for many rejections are planted at the inception of a project, in the form of topics that—no matter how well executed—will not sufficiently appeal to AMJ’s reviewers and readers. Likewise, many manuscripts ultimately earn revise-and-resubmits as a result of topic choices that gave them clear momentum, right out of the gate. What is the anatomy of a topic that, in our opinion, creates that sort of momentum at AMJ? Our editorial will focus on five distinct criteria of effective topics: significance, novelty, curiosity, scope, and actionability.
Significance: Taking on “Grand Challenges”
A starting point to consider when selecting a topic is whether the study confronts or contributes to a grand challenge. The term “grand challenge” is credited to a mathematician, David Hilbert, whose list of important unsolved problems has encouraged innovation in mathematics esearch since the turn of the 20th century. Grand challenges have been applied to diverse fields in the natural sciences, engineering, and medicine. Examples of grand challenges used by the United States National Academy of Engineering include engineering better medicines and making solar energy economical. The grandest of these challenges are reflected in the United Nations Millennium Development Goals to eradicate global poverty, disease, and hunger. The fundamental principles underlying a grand challenge are the pursuit of bold ideas and the adoption of less conventional approaches to tackling large, unresolved problems.
Of course, few AMJ submissions will deal with topics as globally significant as reducing poverty or combating hunger. What AMJ submissions can do is deal with large, unresolved problems in a particular literature or area of inquiry and tackle those problems in a bold and unconventional way that leaps beyond existing explanations. Often that leap will engender new paradigms or open new pastures for scholarly discourse. For example, Ferlie, Fitzgerald, Wood, and Hawkins (2005) took on a grand challenge in asking why evidence-based innovations failed to sspanad in the health care industry. Innovation diffusion is an issue of vital importance in a number of literatures, and the focus on health care innovations lent additional weight to the topic. Ferlie et al. (2005) then confronted the topic in a bold and unconventional way by going beyond linear models of diffusion and arguing that factors that could seemingly aid diffusion— such as professionalization— could instead create “nonsspanad.”
This conceptualization of grand challenges provides a crucible for melding discussions of theoretical usefulness and the broader perspective that individual and societal benefit can accrue from economic and entrespanneurial activity (Brief & Dukerich, 1991; Ghoshal, Bartlett, & Moran, 1999; Schumpeter, 1942; Sen, 1999). Understandably, every topic choice cannot introduce a new paradigm; the cumulativeness of scholarship and the progress of social sciences require us to build on prior work. Moreover, the “grandness” of unresolved problems will vary from literature to literature over time. Nonetheless, posing each topic within a grand challenge framework provides voice to a study’s raison d’eˆtre; it allows the author to articulate how the study solves a piece of a larger puzzle, and in so doing, moves the field forward with rigor and relevance (Gulati, 2007).
Novelty: Changing the Conversation
Like many other top journals, AMJ also emphasizes novelty in topic choice. Given that scientific work can be viewed as a conversation among scholars (Huff, 1998), one simple way to check the novelty of a topic is to consider whether a study ad-dressing it would change the conversation that is already taking place in a given literature. Does the study merely add to the momentum created by existing voices, or does it cause heads to turn as the conversation darts in an entirely new direction? Sometimes that new direction is created by adding new vocabulary to the conversation, in the form of new ideas or constructs, and sometimes that new direction results simply from new insights not articulated by prior voices.
Novel topics can often result from knowledge recombination, with something “new” being created by building a bridge between two literatures or disciplines. Fields that draw from within themselves for extensions of ideas tend to become more insular over time, reducing the likelihood that novel solutions will emerge (George, Kotha, & Zheng, 2008). The organizational theory and strategy literatures often refer to “knowledge recombination” as a way to generate new ideas. The spanmise is that organizations generate new and creative solutions by exploring new technological domains for inspiration and recombining the ideas that emerge with knowledge already resident in the organizations (e.g., March, 1991; Rosenkopf & Nerkar, 2001). In extensions of this argument, Ahuja and Lampert (2001) found that organizations must overcome three pathologies of learning to create novel breakthroughs: the tendency to favor the familiar over the unfamiliar, the tendency to spanfer the mature to the nascent, and the tendency to spanfer solutions that are near to existing approaches, rather than completely new.
These three pathologies—dubbed “the familiarity trap,” “the maturity trap,” and “the nearness trap”—become worthy considerations when choosing a topic for AMJ. Picking a topic that is too familiar may result in a study that is perceived, at best, as a marginal extension of an existing conversation. Picking a topic that is too mature raises concerns about a contribution that is viewed as too redundant. Similarly, topic choices that respansent spaces adjacent to existing literatures could be seen as too overlapping and as departing radically enough from existing perspectives on the core phenomenon. Agarwal, Echambadi, Franco, and Sarkar’s (2004) study of “spin-outs” respansents a topic that avoids the familiarity, maturity, and nearness traps. Spin-outs are entrespanneurial ventures started by former employees of a firm that go on to compete in the same space as that firm using knowledge gained from its history. Agarwal et al.’s (2004) study changed the conversation in the entrespanneurship and capabilities literatures by focusing attention on a new and underresearched phenomenon.
Curiosity: Catching and Holding Attention
Although a novel topic may draw a reader in, it takes something more to catch and hold their attention. The best topics for AMJ spark and maintain curiosity. In this context, curiosity can be seen as an approach-oriented motivational state that is associated with deeper, more persistent, and more immersive processing of information (Kashdan & Silvia, 2009). Davis’s (1971) “index of the interesting” is one useful way to describe how to arouse a reader’s curiosity. According to Davis (, topics are interesting when their propositions counter a reader’s taken-for-granted assumptions. For example, a study focused on showing a seemingly good phenomenon to be bad would arouse curiosity because it challenges the reader’s initial expectations.
Another way to think about arousing and maintaining curiosity is to use mystery as a metaphor. Alvesson and Ka¨rreman (2007) argued that interesting research topics flow out of “breakdowns”: surprising findings in one’s own data or the extant literature that cannot be explained by methodological issues or existing explanations. Breakdowns provide an opportunity for scholars to use their imagination, and they signal the potential existence of a mystery: “When asking more questions, hanging around . . . and walking to the library and reading more books fails to be sufficient, a mystery is at hand” (Alvesson & Ka¨rreman, 2007: 1272). Interesting topic choices then arise out of a desire to solve or reformulate the mystery. Such topics are believed to arouse more interest than the more typical “gap-spotting” approach to generating research questions (Alvesson & Sandberg, 2011).
Indeed, we can carry the mystery metaphor one step further by considering why mystery novels are so absorbing and engaging. Consider Agatha Christie’s And Then There Were None, wherein ten guests find themselves trapped on an island mansion before being murdered, one-by-one, in accordance with the “Ten Little Soldiers” nursery rhyme. The story is a page-turner for one simple reason: the reader does not know the ending. Unfortunately, the ending of many AMJ submissions is clear and obvious from the title on, even without the “spoilers” provided in the typical academic abstract, because only one conclusion seems plausible. Consider this title: “The Effects of Leader Displays of Happiness on Team Performance.” A reviewer could guess the contents of the ending—or, at least, the contents of the Results section—because of the intuitive nature of the topic. A study by Van Kleef, Homan, Beersma, van Knippenberg, van Knippenerg, and Damen (2009) aroused significantly more curiosity. Motivated by inconsistent findings about the effects of positive and negative leader displays of emotion, the authors examined whether team performance would be facilitated by leaders displaying happiness or by leaders displaying anger. They also examined whether those effects could be explained by follower emotions (“searing sentiments”) or by follower inferences about performance (“cold calculations”). Which leader display is more effective, and which mechanism explains the results? If you cannot guess the ending, then the authors made an effective topic choice.
Scope: Casting a Wider Net
Even the best topic ideas can be undermined if the resulting study is too small. Our discussion defines scope as the degree to which the landscape involved in a topic is adequately sampled, in terms of relevant constructs, mechanisms, and perspectives. Studies cannot tackle grand challenges if they are not ambitious in scope, and casting a narrow net limits the investigation of relevant mysteries or gaps in the literature. Submissions may have inadequate scope because authors are under the mistaken imspanssion that AMJ still publishes “research notes.” It does not, and in fact rarely publishes any article that is significantly shorter than the 40 pages (in Microsoft Word) given as a guideline in our “Information for Contributors.” Anecdotally, we suspect that other submissions struggle with scope because authors slice their data too thin—trying to get multiple good papers out of a data set rather than one great one.
The best topics set out to fully and comspanhensively sample the landscape in a given domain and may even include constructs and mechanisms derived by using multiple lenses. Seibert, Kraimer, and Liden’s (2001) examination of social capital and career success provides a good example of effective scope in topic choice. Discussions of social capital have pointed to three theoretical perspectives that can explain why the size and composition of an employee’s social network can impact his or her salary, promotability, and career satisfaction. Seibert et al. (2001) could have chosen to focus on the first of those perspectives, or the second, or the third. Instead, they focused on all three perspectives, operationalizing mediators for each of them. Of course, it is possible for a submission to get too big. Those issues can be addressed in a revision, however, as reviewers can suggest dropping variables to bring more focus to a topic.
Actionability: Insights for Practice
Finally, a topic should be actionable: it should offer insights for managerial or organizational practice. One way to approach the actionability criterion is to consider variability in practices that our existing vocabulary of constructs cannot explain—that is, places where our scholarly language or words fail us. For example, the innovation literature typically paints innovation as the result of capital-intensive research and development efforts. How, then, can we explain emergent innovations that have low capital intensity, severely restricted research and development spending, yet still create value? Products such as a $20 artificial knee and low-cost medical equipment remain “white spaces” in both a competitive and academic sense.The academic study of such topics therefore has an inherent actionability.
McGahan (2007) states five major ways that management studies can be actionable: (1) offering counterintuitive insights, (2) highlighting the effect of new and important practices, (3) showing inconsistencies in, and consequences of, practices, (4)suggesting a specific theory to explain an interesting and current situation, and (5) identifying an iconic phenomenon that opens new areas of inquiry and practice. All five of these pathways are spansent when topics respansent grand challenges and when their pursuit is ambitious in scope and offers novel and unconventional changes to existing conversations. Vermeulen (2007) offers a complementary perspective, noting that research has relevance when it can generate insights that practitioners find useful for understanding their own organizational realities, especially if it concerns variables that are within the control of managers.
Conclusion
In sum, an effective topic is one that allows researchers to tackle a grand challenge in a literature, pursue a novel direction that arouses and maintains curiosity, build a study with ambitious scope, and uncover actionable insights. The 64 submissions that are currently in the hands of AMJ’s reviewers will fare better if their topics have that anatomy, as opposed to being more modest, incremental, intuitive, narrow, or irrelevant in nature. Given that topic choice is one of the least revisable aspects of any submission, we would urge any future submitter to ask frank and critical colleagues for feedback on their topic choices—especially if those colleagues are familiar with AMJ. Doing so can help those topics achieve a momentum that will be helpful down the road, once the manuscript is in the hands of reviewers.
Jason A. Colquitt
University of Georgia
Gerard George
Imperial College London
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