ساخت سوالات پژوهش در مدیریت پروژه
|کد مقاله||سال انتشار||مقاله انگلیسی||ترجمه فارسی||تعداد کلمات|
|3320||2012||13 صفحه PDF||سفارش دهید||محاسبه نشده|
Publisher : Elsevier - Science Direct (الزویر - ساینس دایرکت)
Journal : International Journal of Project Management, Volume 30, Issue 7, October 2012, Pages 804–816
This article examines how opportunities for contributions are created in project research. In the article the arguments that underlie research question constructions are analyzed and their role in theory construction is reflected upon. The analysis is based upon a review of 61 papers published between 2007 and 2011 in the four major project management outlets. The results show that questions identify gaps and extend literature rather than challenge the theoretical assumptions. It is argued that the dominance of “gap spotting” hampers the development of the project field by producing theories that do not challenge long-held, sometimes possibly false, assumptions. Researchers are therefore urged to become bolder in their claims, some suggestions on how to achieve this are offered.
With the proliferation of papers dealing with projects in the top-tier management journals, the recent birth of new dedicated project management journals, the inclusion of the established project journals in the Social Science Citation Index and an increased industry diffusion creating a tremendous impact in working practices, it is about time to examine how opportunities for contributions are created in project research. Research questions are fundamental in that they set the scope, aim or contribution to academia or to practice. Well-grounded and carefully formulated research questions may extend old ideas and develop new ideas. Simply, the kinds of research questions that are asked determine what theories are eventually produced. Despite the importance of research questions in scholarly work there is little guidance regarding their construction. Textbooks on research methodology do “not provide more specific directions on ways to formulate innovative research questions by scrutinizing existing literature in a particular research area” (Sandberg and Alvesson, 2011:24), beyond that it should be clearly defined in terms of topic, domain and object of study, etc. (e.g. Silverman, 2001). Other efforts come closer. For example, Davis (1971) focused on what made qualitative theories interesting1 and famous. Interesting papers, Davis argues, are the ones that refute some, but not all, of the particular audience's assumptions. Similar efforts have targeted how contributions are framed as contributing to specific areas. Here Locke and Golden-Biddle (1997) dealt with how researchers create opportunities to contribute to the literature, identifying associated rhetorical practices in top American journals. Criticizing previous efforts for not considering how research questions are constructed, Sandberg and Alvesson (2011) studied research question construction in the top four American and top European management journals. They found that none of the 52 investigated papers attempted to invoke new theories. This debate has so far concentrated on organization, management theory and A-level journals or the stakeholders of an interesting theory. Consequently, the debate has made important contributions to the understanding of how opportunities are created to contribute to the literature, or how research questions are constructed in established areas where top-tier journals make demands for theoretical contributions and scientific rigor that are undoubtedly higher than in journals in less established areas such as project management. As a young subfield of management, project management is relatively immature compared to general organization theory. Project management journals are neither recognized as A-level journals outside of the field (c.f. www.harzing.com), nor do they demand a similar focus on theoretical developments from their authors. Papers in such subfields thus face different challenges in terms of theoretical contributions, including the development of a coherent field, associated to the pre-paradigmatic state of project research (Bredillet, 2010). Meanwhile, most publications in academia generally are not within the top-tier journals. How contributions to project journals are framed not only contributes to the field as such but also provides important linkages to the extensive scholarly interest in projects as a new organizational form outside of the immediate project literature realm (Söderlund, 2010:2). This leaves a void in knowledge about how opportunities for contributions are framed in journals below the A-level. The present paper, drawing upon the typology developed by Sandberg and Alvesson (2011) and Locke and Golden-Biddle (1997), extends the contemporary debate by investigating how researchers in project management construct research questions, as they are expressed in the four major project management journals. The purpose of this paper is to analyze the arguments that underlie the research questions and reflect upon their role in theory construction. Through the review of 61 papers published between 2007 and 2011 in the four major project management outlets, the paper makes four contributions. First, in contrast to the contemporary debate, the paper investigates a subfield of management studies, which gives it a specific thematic focus that may assist in bridging contributions to other management or organization theory areas. Secondly, it examines a less mature area of research with correspondingly few developed theoretical foundations. Thirdly, it provides the basis for an argument that focuses on the construction of research questions, in order to develop insights about project management. Finally, the paper highlights the possibility of different approaches to constructing research questions in order to produce theories. 1.1. Developing theories for and of project research A theory constitutes “an ordered set of assertions about a generic behavior or structure assumed to hold throughout a significantly broad range of specific instances” (Sutherland, 1975:9, cited in Weick, 1989:517). There have been many attempts to find and develop such theories of project management aiming at creating theories or a unifying theory for project research on which to build and gain further acceptance ( Andersen, 2006, Artto and Wikstrom, 2005, Jugdev, 2004, Leybourne, 2007, Lundin and Söderholm, 1995, Peippo-Lavikka et al., 2011, Shenhar and Dvir, 1996, Turner, 2006a, Turner, 2006b, Turner, 2006c and Turner, 2006d). The general idea is that a theory of projects is beneficial to the development and acceptance of the field for a general audience. The state of project theory has however been the subject of continual debate for several years. Essentially, research that ranges from instrumental research on models to studies of processes has been found overly rational and instrumental (Cicmil and Hodgson, 2006 and Packendorff, 1995) and there is therefore a claimed need to “reclaim” (Blomquist et al., 2010 and Hällgren and Söderholm, 2011) and “re-think project management” and “examine how current theories, concepts and methodologies underpinning project management research could be enriched and extended to enhance the relevance of the knowledge created in the research process” (Winter et al., 2006:646). Regardless of one's point of view about the need for one or several theories of projects, a unified field of research does not yet exist. Project research is therefore in a pre-paradigmatic state (Bredillet, 2010). Attempts to provide overviews to continue the construction of project management as a field have described it as having different schools. For example, based on publications in the major project management outlets, Bredillet, 2007a, Bredillet, 2007b, Bredillet, 2007c, Bredillet, 2008a, Bredillet, 2008b and Bredillet, 2008c describes nine schools with different theoretical emphases. Söderlund (2010) on the other hand, focuses on the project literature published in higher-level journals outside of the immediate project realm. The schools, Söderlund argues, demonstrate a rather high diversity among theoretical approaches and some of the assumptions, when compared, may further understanding of project research. 1.2. The face of Janus in theory development Janus is the two-faced Roman god who looks simultaneously into the future and the past. In the discourse surrounding management research (Alvesson and Sandberg, 2011, Johnson, 2003 and Tadajewski and Hewer, 2011) and in the practice of journal paper acceptance (Bedeian, 2003 and Bedeian, 2004), future-looking innovative research is especially valued, for the simple reason that innovative ideas, whose conclusions have maintained relevance and validity, (Bartunek et al., 2006:10), have the power to challenge long-held seemingly unproblematic assumptions. (cf. Locke and Golden-Biddle, 1997:1025) Davis asserted that those theorists “who carefully and exhaustively verify trivial theories are soon forgotten; whereas those who cursorily and expediently verify interesting theories are long remembered” (Davis, 1971:309). An interesting theory, then, is one that denies “certain assumptions of their audience” (Davis, 1971:309). In order to attract the attention of the audience, the theory must be innovative in relation to the theoretical structure that makes up the everyday theoretical life that is present in other writings and their propositions. That said, an interesting theory must also have a practical usefulness, which implies that the findings must challenge and improve common practice (Davis, 1971:311). While Davis targeted an academic audience and scholarly arguments, Bartunek et al. (2006) extended the investigation into empirically based papers in an investigation of what the members of the Academy of Management Journal's editorial board found interesting. The findings largely mirrored those of Davis in that they would have to be counter-intuitive, good quality, well written, include a new theory/finding, have practical implications and make an impact. This paradigm shifting type of theory development tends to be part of what Kuhn (1962/1996) calls revolutionary science. Revolutionary science refers to an epistemological paradigm shift in the scientific community. That is, following a paradigm shift the worldview is changed and there is no return to the former one. Challenging these assumptions, being an inherent part of developing so called interesting theories (Davis, 1971), are bound to meet resistance since there are conventions about the current knowledge paradigm. This is demonstrated in both how research questions are framed (Locke and Golden-Biddle, 1997) and in the journal review process (Bedeian, 2004). The other side to the widely held assumption that future-looking innovative theory development is positive, is that there are negative effects associated with forgetting the past. On the negative side, only trying to overturn existing theory contributes to a mechanized and industrialized type of scholarship that is becoming increasingly inaccessible to practitioners (Tourish, 2011). Furthermore, striving for novelty arguably contributes to fewer comprehensive cross-perspective analyses and thus fewer holistic studies. Moreover, assuming that innovative theory development is positive contributes to fewer replication studies, less common concepts and the fragmentation of the research area, which thus looses explanatory power. The important consequence of less integration and less replication is that theories are hampered in their development (Mone and McKinley, 1993:292–293). The possibility of replication in social sciences is debated, but Tsang and Kwan argue that a replication of a theory may significantly raise its credibility and hence contribute to development of the field (Tsang and Kwan, 1999:776). Similarly Glynn and Raffaelli (2010) argue, with evidence from the leadership literature, that the there is a great danger from both sides of the faces of Janus. Therefore they suggest that any attempt to develop a field has to rely on both a diversification and a novel approach to theory development. This is echoed by Colquitt and George (2011) in their editorial in the Academy of Management Journal, although still with a clear preference for recombination of fields to produce novel results. In the words of Kuhn this tends to be inclined to normal science. Normal science refers to “research firmly based upon one or more past scientific achievements, achievements that some particular scientific community acknowledges for a time as supplying the foundation for its further practice” (Kuhn, 1962/1996:10). Thus, normal science tends to relate to the epistemological relation of past science, and revolutionary science to the epistemological relation of mind shifting future-oriented science. 1.3. The construction of research questions Investigating scientific texts to understand the underlying process is not new (Davis, 1971, Johnson, 2003 and Mathiassen et al., 2011). These studies are focused on the “interesting” aspect of paper construction rather than paying attention to the construction of the research question. With more interest in the construction of research, Locke and Golden-Biddle (1997) reviewed 82 qualitative papers in Administrative Science Quarterly and Academy of Management Journal to assess how they created opportunities for theoretical contributions. They found that there were two main arguments used—structuring inter-textual coherence and problematization. The structured inter-textual coherence refers to a writing practice that in large part reflects the coherence or incoherence of the previous work. Problematization, by contrast, refers to deficiencies in the present theorizing—deficiencies that have to be remedied. Building and extending upon Locke and Golden-Biddle (1997) by focusing on the research question construction per se and its ability to create opportunities for theory development, Sandberg and Alvesson reviewed 52 papers in Administrative Science Quarterly, Journal of Management Studies, Organization studies, and Organization. They identified three main modes: confusion spotting, neglect spotting and application spotting. The first mode, confusion spotting, “spot[s] some kind of confusion in existing literature” (Sandberg and Alvesson, 2011:29), where the evidence from the literature is not clear and is typically contradictory. The research question, therefore, is constructed from the literature by looking for competing explanations in relation to prior research. The second mode, neglect spotting, argues that there is an academically uncharted area requiring attention and analysis. A majority of the 52 papers in Sandberg and Alvesson's sample were characterized by neglect spotting. Neglect spotting comes in three versions: an overlooked area; an under-researched area; or a lack of empirical support. The most common argument was based on the overlooking of a certain area, essentially that the area is developed but lacks a specific focus. An under-researched area is one in which there is a strong bias towards a certain perspective, leaving other areas under-researched. The third version of neglect spotting refers to work that argues for the existence of theoretical concepts and models but in which there is an empirical lack of support that warrants further investigation. The third and final way of spotting a gap is application spotting, which argues that an area of research lacks a particular theory or perspective and “that a specific body of literature needs to be extended or complemented in some way or another” (Sandberg and Alvesson, 2011:31). It is common to combine these approaches because of how research questions are developed but usually one of them is dominant. While not frequently used, problematization refers to a way of constructing the research question that “aims to question the assumptions underlying existing theory in some significant ways” (Sandberg and Alvesson, 2011:32). Although gap spotting challenges existing knowledge, it should therefore not be mistaken for problematization, which denies a significant part of the present knowledge. Consequently, problematization of a genre does not require a paradigm shift that overturns the understanding of something in a Kuhnian sense (1962/1996). Problematization-based research focuses on the problems with a particular area of research rather than issues that remain to be researched, and examines what is potentially problematic with the assumptions with some research rather than building positively on its contributions. Four ways of going beyond gap spotting have been identified (Alvesson and Sandberg, 2011): critical confrontation; new idea; quasi-problematization, and problematization. All but the last of these refer to more problematizing modes. Critical confrontation challenges the assumptions underlying a certain area, which is the case in most critical research studies. New idea refers to the construction of a research question that is original, despite being based on the shortcomings of existent theory. Quasi-problematization infuses pre-developed alternatives in what is referred to as problematization (but hence really is not). Finally, problematization constructs the research question through carefully developed logic-breaking arguments that go beyond the application of a particular theoretical, empirical or methodological approach. In this paper no explicit paradigmatic stance is taken except that paradigm shifts tend to emerge rarely. To summarize, the frameworks discussed above provide an analytical pattern that are drawn upon in order to understand how opportunities for theoretical contributions are constructed through the framing of research questions.
نتیجه گیری انگلیسی
Theorists are not remembered for having carefully chiseled out extensions of existing theories. Nor are great theories achieved without challenging basic assumptions. Without the careful chiseling research areas however run the risk of losing its credibility. Nevertheless, the research question is an integrated part of either craftsmanship. Since the research questions' constructions were reviewed with reference to how they were expressed in the papers' texts, the present paper cannot say anything about how the research question was constructed beyond that text. Therefore, the analysis is limited to what is written. Neither does this paper focus upon whether the results were “interesting” per se, but merely upon the created opportunities for becoming interesting. With a sample of 61 papers between 2007 and 2011 from two issues each of the leading four project management journals, the paper also runs the risk of missing more assumption-challenging papers and books in project research since they tend to come about rarely. The selected papers do however reflect the status of general project research as provided in the sample. Finally, novel ideas may emerge in books. Journals are however still the premium outlet for research and they are tightly integrated into academic advancement (Pfeffer, 2007) and the review process explicitly reflects the paradigmatic struggle (Bedeian, 2004). Without a specific focus on identifying novel ideas an analysis of journal papers seem appropriate. With these limitations in mind, some reflections seem in order. The present study's review of the research question argument found that similar to research in leading management journals, project management research is focused on gap spotting and no paper problematized the foundations of project research. Compared to Sandberg and Alvesson's (2011) typology of research question construction modes, the distribution between the papers was fairly homogenous. However, two additional categories were identified: empirical example or need, and research overview. While overviews do not seem representative of the distribution of papers in general, the finding of the “empirical example or need” category suggests that project research still relies to a great extent on the heritage of practically oriented research. Since a lack of a research question, a research purpose or both was over-represented in the sample, it is possible that greater potential could be generated if the research question were constructed more from a theoretical point of view and on making contributions that follow from that. From the findings that an overwhelming dominance of gap spotting arguments relies on existing theory and its assumptions, project research has a tendency to re-emphasize the underlying assumptions of previous research. Re-emphasizing previous understandings is of course important in terms of establishing a field's credibility but it simultaneously hampers its further development and diffusion as well as its acceptance by a general audience.